The Handbook of Experimental Economics, Volume 2: The Handbook of Experimental Economics 9781400883172

Table of contents :
Contents
Preface
Chapter 1 Macroeconomics: A Survey of Laboratory Research
1. Introduction: Laboratory Macroeconomics
2. Dynamic, Intertemporal Optimization
2.1. Optimal Consumption/Savings Decisions
2.2. Exponential Discounting and Infinite Horizons
2.3. Exponential or Hyperbolic Discounting?
2.4. Expectation Formation
3. Coordination Problems
3.1. Poverty Traps
3.2. Bank Runs
3.3. Resolving Coordination Problems: Sunspots
3.4. Resolving Coordination Problems: The Global Game Approach
4. Fields in Macroeconomics
4.1. Monetary Economics
4.2. Labor Economics
4.3. International Economics
4.4. Multisectoral Macroeconomics
5. Macroeconomic Policies
5.1. Ricardian Equivalence
5.2. Commitment versus Discretion
5.3. Monetary Policy
5.4. Fiscal and Tax Policies
6. Conclusions
Acknowledgments
Notes
References
Chapter 2 Using Experimental Methods to Understand Why and How We Give to Charity
1. Introduction
2. Preferences for Giving
2.1. Is Giving Rational?
2.2. Motives
3. Fundraising
3.1. Announcements: Sequential and Dynamic Giving
3.2. Lotteries
3.3. Auctions
3.4. Rebates and Matches
4. Conclusion
Notes
References
Chapter 3 Neuroeconomics
INTRODUCTION
1. Neurobiological Foundations
1.1. The Cellular Structure of the Brain
1.2. From Neurons to Networks
1.3. Summary of Neurobiology
2. Functional MRI: A Window into the Working Brain
2.1. Functional MRI and the BOLD Signal
2.2. Design Considerations
2.3. Image Analysis
2.4. Summary of Functional MRI
3. Risky Choice
3.1. Statistical Moments
3.2. Prospect Theory
3.3. Causal Manipulations
3.4. Logical Rationality and Biological Adaptation
3.5. Summary of Risky Choice
4. Intertemporal Choice and Self-regulation
4.1. Empirical Regularities
4.2. Multiple-Self Models with Selves That Have Overlapping Periods of Control
4.3. Multiple-Self Models with Selves That Have Nonoverlapping Periods of Control
4.4. Unitary-Self Models
4.5. Theoretical Summary
5. The Neural Circuitry of Social Preferences
5.1. Social Preferences and Reward Circuitry
5.2. Do Activations in Reward Circuitry Predict Choices?
5.3. The Role of the Prefrontal Cortex in Decisions Involving Social Preferences
5.4. Summary
6. Strategic Thinking
6.1. Strategic Awareness
6.2. Beliefs, Iterated Beliefs, and Strategic Choice
6.3. Learning
6.4. Strategic Teaching and Influence Value
6.5. Discussion of Strategic Neuroscience
6.6. Summary
7. Conclusion
Acknowledgments
Notes
References
Chapter 4 Other-Regarding Preferences: A Selective Survey of Experimental Results
INTRODUCTION
I. Where Things Stood Circa 1995
II. Models of Other-Regarding Preferences, Theory, and Tests
A. Outcome-Based Social Preference Models
B. Some Initial Tests of the Bolton-Ockenfels and Fehr-Schmidt Models
C. Social Preferences versus Difference Aversion
D. Models Incorporating Reciprocity/Intentions of Proposers
E. Other-Regarding Behavior and Utility Maximization
F. Learning
III. Other-Regarding Behavior, Applications, and Regularities
A. The Investment/Trust Game
B. Results from Multilateral Bargaining Experiments
C. A Second Look at Dictator Games
D. Procedural Fairness
E. Diffusion of Responsibility
F. Group Identity and Social Preferences
G. Generalizability
IV. Gift Exchange Experiments
A. An Initial Series of Experiments
B. Incomplete Contracts
C. Wage Rigidity
D. The Effect of Cognitive Ability and the Big Five Personality Characteristics in Other-Regarding Behavior
E. Why Does Gift Exchange Occur?
F. Laboratory versus Field Settings and Real Effort
G. Summary
V. Conclusions
Acknowledgments
Notes
References
Chapter 5 Experiments in Market Design
1. Introduction
2. Some Early Design Experiments: Allocation of Airport Slots
3. FCC Spectrum Auctions
4. Other Auctions
4.1. eBay Auctions
4.2. A Poorly Designed Auction (for Medicare Supplies)
5. Labor Market Clearinghouses
5.1. Designing Labor Markets for Doctors
5.2. Matching without a Clearinghouse: The Market for Economists, and Online Dating
6. Course Allocation
7. Conclusions
Notes
References
Chapter 6 Experiments in Political Economy
1. Introduction and Overview
1.1. Methodology: Relationship to Experimental Economics
1.2. Chapter Road Map
2. Experiments in Committee Bargaining
2.1. Unstructured Committee Bargaining
2.2. Committee Bargaining with a Fixed Extensive Form Structure
3. Elections and Candidate Competition
3.1. The Spatial Model of Competitive Elections and the Median Voter Theorem
3.2. Multicandidate Elections
3.3. Candidate Competition with Valence
4. Voter Turnout
4.1. Instrumental Voting Experiments
4.2. The Effects of Beliefs, Communication, and Information on Turnout
4.3. Expressive Voting Experiments
5. Information Aggregation in Committees
5.1. Condorcet Jury Experiments
5.2. The Swing Voter’s Curse
6. Voting Mechanisms that Reflect Preference Intensity
6.1. Mechanisms Where a Budget of Votes Can Be Allocated Across Issues
6.2. Vote Trading and Vote Markets
7. Where Do We Go From Here?
Acknowledgments
Notes
References
Chapter 7 Experimental Economics across Subject Populations
I. Introduction
II. Infrahumans
II.A. Methodological Notes
III. Children
III.A. Methodological Notes
IV. Token Economies
IV.A. Methodological Notes
V. Elderly
V.A. Methodological Notes
VI. Highly Demographically Varied (Representative) Sample
VI.A. Methodological Notes
VII. Subjects with Relevant Task Experience
VII.A. Methodological Notes
VIII. Discussion
VIII.A. Individual Choice
VIII.B. Games
IX. Conclusion
Acknowledgments
Notes
References
Chapter 8 Gender
I. Introduction
II. Gender Differences in Competitiveness
II.A. Do Women Shy Away from Competition?
II.B. Replication and Robustness of Women Shying Away from Competition
II.C. Reducing the Gender Gap in Tournament Entry
II.D. Performance in Tournaments
II.E. Field Experiments on Gender Differences in Competitiveness
II.F. External Relevance of Competitiveness
III. Gender Differences in Selecting Challenging Tasks and Speaking Up
III.A. Gender Differences in Task Choice
III.B. Gender Differences in Speaking up
IV. Altruism and Cooperation
IV.A. Dictator-Style Games
IV.B. Field Evidence and External Relevance of Gender Differences in Giving
IV.C. Prisoner’s Dilemma and Public Good Games
IV.D. New Directions
IV.E. Conclusions
V. Risk
V.A. Early Work and Surveys by Psychologists
V.B. Early and Most Commonly Used Elicitation Methods in Economics
V.C. Early Economic Surveys
V.D. Recent Economic Surveys and Meta-Analyses on Specific Elicitation Tasks
V.E. Stability of Risk Preferences and Their External Relevance
V.F. An Example of a Careful Control for Risk Aversion
V.G. Conclusions
VI. Conclusions
Acknowledgments
Notes
References
Chapter 9 Auctions: A Survey of Experimental Research
INTRODUCTION
I. Single-Unit Private Value Auctions
1.1. Bidding above the RNNE in First-Price Private Value Auctions
1.2. Bidding above the RNNE and Regret Theory
1.3. Using Experimental Data to Corroborate Maintained Hypotheses in Empirical Applications to Field Data
1.4. Second-Price Private Value Auctions
1.5. Asymmetric Private Value Auctions
1.6. Sequential Auctions
1.7. Procurement Auctions
1.8. Cash-Balance Effects and the Role of Outside Earnings On Bids
1.9. An Unresolved Methodological Issue
II. Single-Unit Common Value Auctions
2.1. English Auctions
2.2. Auctions with Insider Information
2.3. Common Value Auctions with an Advantaged Bidder
2.4. New Results in the Takeover Game: Theory and Experiments
2.5. Additional Common Value Auction Results
2.6. Is the Winner’s Curse Confined to College Sophomores?
III. Multiunit-Demand Auctions
3.1. Auctions with Homogeneous Goods—Uniform Price and Vickrey Auctions
3.2. More on Multiunit-Demand Vickrey Auctions
3.3. Auctions with Synergies
3.4. Sequential Auctions with Multiunit-Demand Bidders
IV. Additional Topics
4.1. Collusion in Auctions
4.2. Bidder’s Choice Auctions: Creating Competition Out of Thin Air
4.3. Internet Auctions
4.4. Entry into Auctions
V. Summary and Conclusions
Acknowledgments
Notes
References
Chapter 10 Learning and the Economics of Small Decisions
INTRODUCTION
1. The Basic Properties of Decisions from Experience
1.1. Six Basic Regularities and a Model
1.2. The Effect of Limited Feedback
1.3. Two Choice-Prediction Competitions
2. Dynamic Environments
2.1. The Partial Reinforcement Extinction Effect and Reinforcement Schedules
2.2. Spontaneous Alternation, the Gambler Fallacy, and Response to Patterns
2.3. Negative and Positive Transfer
2.4. The Effect of Delay and Melioration
2.5. Models of Learning in Dynamic Settings
3. Multiple Alternatives and Additional Stimuli
3.1. Successive Approximations, Hill Climbing, and the Neighborhood Effect
3.2. Learned Helplessness
3.3. Multiple Alternatives with Complete Feedback
3.4. The Effect of Additional Stimuli (Beyond Clicking)
4. Social Interactions and Learning in Games
4.1. Social Interactions Given Limited Prior Information
4.2. Learning in Constant-Sum Games with Unique Mixed-Strategy Equilibrium
4.3. Cooperation, Coordination, and Reciprocation
4.4. Fairness and Inequity Aversion
4.5. Summary and Alternative Approaches
5. Applications and the Economics of Small Decisions
5.1. The Negative Effect of Punishments
5.2. The Enforcement of Safety Rules
5.3. Cheating in Exams
5.4. Broken Windows Theory, Quality of Life, and Safety Climate
5.5. Hand Washing
5.6. The Effect of the Timing of Warning Signs
5.7. Safety Devices and the Buying-Using Gap
5.8. The Effect of Rare Terrorist Attacks
5.9. Emphasis-Change Training, Flight School, and Basketball
5.10. The Pat-on-the-Back Paradox
5.11. Gambling and the Medium-Prize Paradox
5.12. The Evolution of Social Groups
5.13. Product Updating
5.14. Unemployment
5.15. Interpersonal Conflicts and the Description-Experience Gap
5.16. Implications for Financial Decisions
5.17. Summary and the Innovations-Discoveries Gap
6. Conclusion
Acknowledgments
Notes
References
Editors and Contributors
Illustration Credits
Name Index
Subject Index

Citation preview

THE HANDBOOK OF EXPERIMENTAL ECONOMICS VOLUME 2

THE HANDBOOK OF EXPERIMENTAL ECONOMICS Volume 2

Edited by John H. Kagel and Alvin E. Roth

PRINCETON UNIVERSITY PRESS PRINCETON AND OXFORD

Copyright © 2015 Princeton University Press Published by Princeton University Press, 41 William Street, Princeton, New Jersey 08540 In the United Kingdom: Princeton University Press, 6 Oxford Street, Woodstock, Oxfordshire OX20 1TR press.princeton.edu Jacket image courtesy of Shutterstock All Rights Reserved ISBN 978-0-691-13999-9 Library of Congress Control Number: 2016935744 British Library Cataloging-in-Publication Data is available This book has been composed in Minion Pro and Myriad Pro Printed on acid-free paper. ∞ Typeset by Nova Techset Pvt Ltd, Bangalore, India Printed in the United States of America 1 3 5 7 9 10 8 6 4 2

CONTENTS Preface xiii

Chapter 1 Macroeconomics: A Survey of Laboratory Research

1

John Duffy 1.

Introduction: Laboratory Macroeconomics 1

2. Dynamic, Intertemporal Optimization 4 2.1. Optimal Consumption/Savings Decisions 4 2.2. Exponential Discounting and Infinite Horizons 12 2.3. Exponential or Hyperbolic Discounting? 13 2.4. Expectation Formation 14 3. Coordination Problems 21 3.1. Poverty Traps 21 3.2. Bank Runs 24 3.3. Resolving Coordination Problems: Sunspots 27 3.4. Resolving Coordination Problems: The Global Game Approach 30 4. Fields in Macroeconomics 32 4.1. Monetary Economics 33 4.2. Labor Economics 46 4.3. International Economics 50 4.4. Multisectoral Macroeconomics 55 5. Macroeconomic Policies 61 5.1. Ricardian Equivalence 61 5.2. Commitment versus Discretion 64 5.3. Monetary Policy 67 5.4. Fiscal and Tax Policies 73 6. Conclusions 78 Acknowledgments 79 Notes 79 References 82

Chapter 2 Using Experimental Methods to Understand Why and How We Give to Charity 91 Lise Vesterlund 1. Introduction 91 2. Preferences for Giving 92 2.1. Is Giving Rational? 95 2.2. Motives 97

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3. Fundraising 108 3.1. Announcements: Sequential and Dynamic Giving 109 3.2. Lotteries 119 3.3. Auctions 123 3.4. Rebates and Matches 126 4. Conclusion 131 Notes 133 References 141

Chapter 3

Neuroeconomics 153

Colin F. Camerer, Jonathan D. Cohen, Ernst Fehr, Paul W. Glimcher, and David Laibson 153 1. Neurobiological Foundations 156 1.1. The Cellular Structure of the Brain 156 1.2. From Neurons to Networks 161 1.3. Summary of Neurobiology 164

INTRODUCTION

2. Functional MRI: A Window into the Working Brain 164 2.1. Functional MRI and the BOLD Signal 165 2.2. Design Considerations 166 2.3. Image Analysis 168 2.4. Summary of Functional MRI 171 3. Risky Choice 172 3.1. Statistical Moments 172 3.2. Prospect Theory 172 3.3. Causal Manipulations 175 3.4. Logical Rationality and Biological Adaptation 176 3.5. Summary of Risky Choice 177 4. Intertemporal Choice and Self-regulation 177 4.1. Empirical Regularities 178 4.2. Multiple-Self Models with Selves That Have Overlapping Periods of Control 181 4.3. Multiple-Self Models with Selves That Have Nonoverlapping Periods of Control 182 4.4. Unitary-Self Models 182 4.5. Theoretical Summary 183 5. The Neural Circuitry of Social Preferences 183 5.1. Social Preferences and Reward Circuitry 184 5.2. Do Activations in Reward Circuitry Predict Choices? 186 5.3. The Role of the Prefrontal Cortex in Decisions Involving Social Preferences 186 5.4. Summary 188 6. Strategic Thinking 189 6.1. Strategic Awareness 189 6.2. Beliefs, Iterated Beliefs, and Strategic Choice 190

Contents

6.3. 6.4. 6.5. 6.6.

7.

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Learning 192 Strategic Teaching and Influence Value 194 Discussion of Strategic Neuroscience 196 Summary 199

Conclusion 200 Acknowledgments 200 Notes 201 References 202

Chapter 4 Other-Regarding Preferences: A Selective Survey of Experimental Results 217 David J. Cooper and John H. Kagel 217 Where Things Stood Circa 1995

INTRODUCTION

I.

218

II. Models of Other-Regarding Preferences, Theory, and Tests 222 A. Outcome-Based Social Preference Models 222 B. Some Initial Tests of the Bolton-Ockenfels and Fehr-Schmidt Models 225 C. Social Preferences versus Difference Aversion 231 D. Models Incorporating Reciprocity/Intentions of Proposers 233 E. Other-Regarding Behavior and Utility Maximization 235 F. Learning 236 III. Other-Regarding Behavior, Applications, and Regularities 240 A. The Investment/Trust Game 240 B. Results from Multilateral Bargaining Experiments 242 C. A Second Look at Dictator Games 244 D. Procedural Fairness 247 E. Diffusion of Responsibility 249 F. Group Identity and Social Preferences 253 G. Generalizability 255 IV. Gift Exchange Experiments 259 A. An Initial Series of Experiments 259 B. Incomplete Contracts 261 C. Wage Rigidity 262 D. The Effect of Cognitive Ability and the Big Five Personality Characteristics in Other-Regarding Behavior 264 E. Why Does Gift Exchange Occur? 265 F. Laboratory versus Field Settings and Real Effort 267 G. Summary 274 V. Conclusions 274 Acknowledgments 276 Notes 277 References 282

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Chapter 5

Experiments in Market Design

290

Alvin E. Roth 1. Introduction 290 2. Some Early Design Experiments: Allocation of Airport Slots 295 3. FCC Spectrum Auctions 300 4. Other Auctions 307 4.1. eBay Auctions 307 4.2. A Poorly Designed Auction (for Medicare Supplies) 316 5. Labor Market Clearinghouses 318 5.1. Designing Labor Markets for Doctors 318 5.2. Matching without a Clearinghouse: The Market for Economists, and Online Dating 327 6. Course Allocation 329 7. Conclusions 333 Notes 334 References 339

Chapter 6

Experiments in Political Economy 347

Thomas R. Palfrey 1. Introduction and Overview 347 1.1. Methodology: Relationship to Experimental Economics 348 1.2. Chapter Road Map 350 2. Experiments in Committee Bargaining 352 2.1. Unstructured Committee Bargaining 352 2.2. Committee Bargaining with a Fixed Extensive Form Structure 359 3. Elections and Candidate Competition 381 3.1. The Spatial Model of Competitive Elections and the Median Voter Theorem 381 3.2. Multicandidate Elections 387 3.3. Candidate Competition with Valence 390 4. Voter Turnout 392 4.1. Instrumental Voting Experiments 392 4.2. The Effects of Beliefs, Communication, and Information on Turnout 397 4.3. Expressive Voting Experiments 398 5. Information Aggregation in Committees 400 5.1. Condorcet Jury Experiments 400 5.2. The Swing Voter’s Curse 406 6. Voting Mechanisms that Reflect Preference Intensity 410 6.1. Mechanisms Where a Budget of Votes Can Be Allocated Across Issues 411 6.2. Vote Trading and Vote Markets 414 7. Where Do We Go From Here? 418

Contents Acknowledgments 419 Notes 419 References 424

Chapter 7 Experimental Economics across Subject Populations 435 Guillaume R. Fréchette I.

Introduction 435

II. Infrahumans 438 II.A. Methodological Notes 443 III. Children 444 III.A. Methodological Notes 449 IV. Token Economies 449 IV.A. Methodological Notes 451 V. Elderly 451 V.A. Methodological Notes 455 VI. Highly Demographically Varied (Representative) Sample 455 VI.A. Methodological Notes 460 VII. Subjects with Relevant Task Experience 461 VII.A. Methodological Notes 468 VIII. Discussion 468 VIII.A. Individual Choice 469 VIII.B. Games 470 IX.

Conclusion 471

Acknowledgments 472 Notes 472 References 475

Chapter 8 Gender 481 Muriel Niederle I. Introduction 481 II. Gender Differences in Competitiveness 485 II.A. Do Women Shy Away from Competition? 486 II.B. Replication and Robustness of Women Shying Away from Competition 489 II.C. Reducing the Gender Gap in Tournament Entry 492 II.D. Performance in Tournaments 497 II.E. Field Experiments on Gender Differences in Competitiveness 503 II.F. External Relevance of Competitiveness 504 III. Gender Differences in Selecting Challenging Tasks and Speaking Up 507 III.A. Gender Differences in Task Choice 507 III.B. Gender Differences in Speaking up 510 IV. Altruism and Cooperation 512

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IV.A. Dictator-Style Games 515 IV.B. Field Evidence and External Relevance of Gender Differences in Giving

519 IV.C. Prisoner’s Dilemma and Public Good Games IV.D. New Directions 523 IV.E. Conclusions 524

520

V. Risk 525 V.A. Early Work and Surveys by Psychologists 527 V.B. Early and Most Commonly Used Elicitation Methods in Economics 530 V.C. Early Economic Surveys 533 V.D. Recent Economic Surveys and Meta-Analyses on Specific Elicitation Tasks 535 V.E. Stability of Risk Preferences and Their External Relevance 538 V.F. An Example of a Careful Control for Risk Aversion 543 V.G. Conclusions 545 VI. Conclusions 546 Acknowledgments Notes 547 References 553

Chapter 9

547

Auctions: A Survey of Experimental Research 563

John H. Kagel and Dan Levin INTRODUCTION

563

I. Single-Unit Private Value Auctions 564 1.1. Bidding above the RNNE in First-Price Private Value Auctions 565 1.2. Bidding above the RNNE and Regret Theory 568 1.3. Using Experimental Data to Corroborate Maintained Hypotheses in Empirical Applications to Field Data 569 1.4. Second-Price Private Value Auctions 570 1.5. Asymmetric Private Value Auctions 572 1.6. Sequential Auctions 576 1.7. Procurement Auctions 578 1.8. Cash-Balance Effects and the Role of Outside Earnings On Bids 580 1.9. An Unresolved Methodological Issue 581 II. Single-Unit Common Value Auctions 582 2.1. English Auctions 583 2.2. Auctions with Insider Information 587 2.3. Common Value Auctions with an Advantaged Bidder 588 2.4. New Results in the Takeover Game: Theory and Experiments 590 2.5. Additional Common Value Auction Results 592 2.6. Is the Winner’s Curse Confined to College Sophomores? 596 III. Multiunit-Demand Auctions 598 3.1. Auctions with Homogeneous Goods—Uniform Price and Vickrey Auctions 598 3.2. More on Multiunit-Demand Vickrey Auctions 604

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3.3. Auctions with Synergies 605 3.4. Sequential Auctions with Multiunit-Demand Bidders 607

IV. 4.1. 4.2. 4.3. 4.4. V.

Additional Topics 610 Collusion in Auctions 610 Bidder’s Choice Auctions: Creating Competition Out of Thin Air 615 Internet Auctions 617 Entry into Auctions 619

Summary and Conclusions 623 Acknowledgments 623 Notes 623 References 629

Chapter 10 Learning and the Economics of Small Decisions

638

Ido Erev and Ernan Haruvy 638 1. The Basic Properties of Decisions from Experience 641 1.1. Six Basic Regularities and a Model 641 1.2. The Effect of Limited Feedback 663 1.3. Two Choice-Prediction Competitions 665 2. Dynamic Environments 668 2.1. The Partial Reinforcement Extinction Effect and Reinforcement Schedules 668 2.2. Spontaneous Alternation, the Gambler Fallacy, and Response to Patterns 670 2.3. Negative and Positive Transfer 671 2.4. The Effect of Delay and Melioration 671 2.5. Models of Learning in Dynamic Settings 672

INTRODUCTION

3. Multiple Alternatives and Additional Stimuli 672 3.1. Successive Approximations, Hill Climbing, and the Neighborhood Effect 672 3.2. Learned Helplessness 674 3.3. Multiple Alternatives with Complete Feedback 675 3.4. The Effect of Additional Stimuli (Beyond Clicking) 675 4. Social Interactions and Learning in Games 677 4.1. Social Interactions Given Limited Prior Information 678 4.2. Learning in Constant-Sum Games with Unique Mixed-Strategy Equilibrium 680 4.3. Cooperation, Coordination, and Reciprocation 683 4.4. Fairness and Inequity Aversion 687 4.5. Summary and Alternative Approaches 688 5. Applications and the Economics of Small Decisions 688 5.1. The Negative Effect of Punishments 688 5.2. The Enforcement of Safety Rules 689 5.3. Cheating in Exams 691 5.4. Broken Windows Theory, Quality of Life, and Safety Climate 692

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5.5. Hand Washing 692 5.6. The Effect of the Timing of Warning Signs 693 5.7. Safety Devices and the Buying-Using Gap 693 5.8. The Effect of Rare Terrorist Attacks 694 5.9. Emphasis-Change Training, Flight School, and Basketball 695 5.10. The Pat-on-the-Back Paradox 695 5.11. Gambling and the Medium-Prize Paradox 696 5.12. The Evolution of Social Groups 696 5.13. Product Updating 697 5.14. Unemployment 697 5.15. Interpersonal Conflicts and the Description-Experience Gap 698 5.16. Implications for Financial Decisions 699 5.17. Summary and the Innovations-Discoveries Gap 699

6. Conclusion 700 Acknowledgments Notes 701 References 702

701

Editors and Contributors 717 Illustration Credits 721 Name Index 725 Subject Index 737

PREFACE his second volume of the Handbook of Experimental Economics follows some 20 years after the original Handbook. There has been a lot of activity in a number of areas that were not covered in the 1995 Handbook, including the emergence of neuroeconomics, significant growth in macroeconomic experiments, and substantial growth in experiments that support market design research. The goal here is to cover some of these new growth topics and others not covered in the 1995 Handbook as well as to update results in some areas of research (e.g., public goods and auctions) that were covered in 1995. Even more so than in the 1995 Handbook, there is no way to cover the entire field of experimental economics or to exhaustively cover the research areas each chapter addresses. Instead we left it to the authors of each chapter to curate important developments, with a view to reporting on series of experiments that highlight the back and forth between different experimenters, between experimenters and theorists, and between experimenters and practitioners. As in the 1995 Handbook, there is no chapter explicitly devoted to experimental methodology, because we continue to believe that methodological issues are best covered within the context of the substantive research questions under investigation. Also, there are a number of active areas of experimental research, both new and old, that we wish we could have reported on here, but to keep the Handbook manageable, we do not cover them. Most of the experiments reported here consist of laboratory studies, but several chapters report extensively on field experiments devoted to understanding the same or related issues studied in lab experiments, as called for by the questions being investigated. There is considerable back and forth both between lab and field experiments and between experiments and naturally occurring field data. The ultimate goal in all cases is to better understand economic behavior as it relates to economic theory and policy applications, with the emphasis on the role of experiments, lab or field (as well as naturally occurring empirical data), in achieving these goals. Many colleagues have contributed to the Handbook in addition to the chapter writers. Earlier chapter drafts were presented at several conferences at which members of the experimental community were invited to comment on early outlines and drafts of the chapters.1 In addition, each chapter has circulated among specialists to get feedback on the results reported and to identify omissions. To be sure, not all this feedback has been incorporated, but much of it has been included in revising chapter drafts. In what follows we provide a brief overview of the contents of the chapters.

T

Chapter 1: “Macroeconomics: A Survey of Laboratory Research,” by John Duffy This chapter surveys the growing body of macroeconomic experiments over the past 20 years.2 This is both possible and relevant due to changes in macroeconomic modeling that have come to rely more and more on microfoundations. (Analogously, evolutionary biologists can’t conduct experiments directly on the fossil record or on species extinction, but our understanding of evolution is enhanced by experiments on fruit flies and on DNA.) The chapter reviews experiments directed at issues in macroeconomics ranging from intertemporal optimization to how agents form expectations, to resolving the many

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coordination problems inherent to the macroeconomy, and to policy applications. There are efforts to reconcile laboratory outcomes with the field data. For example, experiments show that subjects fail to smooth consumption over their laboratory “lifetime” outcomes, typically overconsuming to begin with, which has a clear correspondence in field data that shows massive undersaving for retirement. In each area covered, gaps in the literature and related problems ripe for experimental investigation are reported. So not only does this chapter provide a summary of experimental macroeconomy research, it points macroeconomists to a number of open research questions that can be studied experimentally.

Chapter 2: “Using Experimental Methods to Understand Why and How We Give to Charity,” by Lise Vesterlund The literature on voluntary giving has grown substantially since the first Handbook, with much research devoted to determining the factors that drive generosity. Indicative of the growth of research in the field, to have a manageable survey, this chapter focuses on why and how people give to charities, using a blend of laboratory and field experiments, along with relevant field data. The chapter covers two broad areas of research. The first part of the chapter focuses on sorting out motives for giving, emphasizing results from creative modifications of the traditional public good and dictator games. Issues under investigation are to what extent giving is intentional and to what extent it results from genuine concern for others (altruism), concern for self (“warm glow”), and mistakes. Experiments are reported that investigate alternative models of charitable giving, and self-image effects for giving.3 The second part of the chapter reviews research on fundraising mechanisms. Fundraising differs from the classic mechanism design problem as the fundraiser’s objective is to maximize contributions (net of expenses), and he or she must rely on voluntary giving. Topics reported on include the potential benefits of announcing early contributions even though this invites free riding on lead contributors, and the benefits of different competitive contribution mechanisms such as lotteries, winnerpay and all-pay auctions. Other fundraising techniques, such as matching and rebating contributions, are also studied. The chapter, especially in the second part, reviews laboratory and field experiments as well as naturally occurring field data related to the same issues.

Chapter 3: “Neuroeconomics,” by Colin Camerer, Jonathan Cohen, Ernst Fehr, Paul Glimcher and David Laibson At the time of the 1995 Handbook, we don’t think anyone would have envisioned that neuroeconomics would so grip the attention of an enthusiastic band of pioneers that it would need to have a chapter devoted to it in the subsequent Handbook. But the field has established itself in the interim and has critical mass and vibrancy, as evidenced by the Society of Neuroeconomics, established in 2004, and the Journal of Neuroscience, Psychology and Economics, which started publication in 2008. The chapter is a team effort by prominent scholars in the field. The chapter provides an introduction to neuroscience along with a summary of research results to date in four areas of neuroeconomics—choice under uncertainty, intertemporal choice and self-regulation, the neural circuitry of social preferences, and strategic thinking. The first section outlines the neurobiological foundations of the research, providing the overall motivation and goals of the research program, along with characterizing the relevant parts of the brain that serve as the seat of various

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types of behavior. This is followed by a discussion of research methods, with a focus on fMRI studies, including exactly what is being measured and how fMRI images are evaluated. Research summaries in each of the four substantive areas covered focus on questions and results in relation to leading economic models in each area that would help to pin down their validity (e.g., with respect to prospect theory, determining if there are different parts of the brain where gains and losses are evaluated). Overall, this is a primer for anyone interested in neuroeconomics (casually or otherwise), along with a discussion of early experimental results. It will be interesting to come back in a decade or two to revisit results in these four research areas and see to what extent these early results have laid the groundwork for economics grounded in biology.

Chapter 4: “Other-Regarding Preferences: A Selective Survey of Experimental Results,” by David J. Cooper and John H. Kagel The study of other-regarding preferences has been intensified in experimental research as it became increasingly clear that the standard economic model of strictly ownincome-maximizing agents fails to account for experimental outcomes for a number of topics (e.g., bargaining, public goods provision, trust and reciprocity, and workplace interactions). Perhaps the best way to view the research reported in this chapter is as an inquiry intended to narrow down what exactly is meant by “other-regarding” preferences. This research has gone hand-in-hand with the growth of behavioral economics, as much of the anomalous experimental behavior has been incorporated into economic models. In turn, these models have suggested new experiments to explore their predictions, which have deepened our understanding the nature of other-regarding preferences. The chapter covers two broad areas of research: The first has to do with research aimed at better understanding early results from bargaining games, many of which were reviewed in the earlier Handbook. Those earlier results led to the development of formal models of other-regarding preferences, which provided the motivation for whole new classes of experiments that would probably not have been considered except for these models. New lines of inquiry compared to those covered in the earlier Handbook concern procedural fairness, delegation of responsibility for unkind behavior, group identity and social preferences, in addition to such staples as the trust and dictator games.4 The second broad area of research involves gift exchange in labor markets, a subfield of “efficiency wage theory,” in which employers offer above-market wages and are in turn rewarded with above-minimum effort. There is considerable discussion of the contributions of both laboratory and field experiments to better understand behavior in this area.

Chapter 5: “Experiments in Market Design,” by Alvin E. Roth When the first volume of the Handbook appeared in 1995, the kinds of economic engineering that have come to be known as market design were just developing. New designs for spectrum auctions and for labor-market clearinghouses were proposed by economists in the 1990s and were adopted and implemented in new forms of market organization. Market design has continued to grow, and much of the chapter focuses on the way experiments have complemented other forms of investigation, not only to explore the underlying science but also to communicate it to the many interested parties among whom new market designs have to be coordinated if they are to be implemented. The chapter considers the various roles that experiments played in the debates surrounding the initial design of auctions for radio spectrum licenses and the continuing

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role they have played in the development of more complicated auctions that allow bidders to bid on packages and not just on individual licenses. It also considers how experiments have played a role in understanding the role of the “hard-close” ending rule in online eBay auctions, in guiding the revision of eBay’s reputation mechanism, in the use of experiments to help design and implement labor market institutions, such as the clearinghouse “Matches” that are used in various markets for doctors, and the signaling mechanism used in the market for new PhD economists. Throughout, the emphasis is on how experiments play a role as one among many tools in bringing a new design from conception through implementation.

Chapter 6: “Experiments in Political Economy.” by Thomas R. Palfrey The focus of this chapter is on political science experiments in the methodological tradition of economic experiments with incentivized subjects and controlled laboratory conditions. The experiments reported are theory driven, dealing with outcomes in nonmarket settings: elections, committees, and so on. The issues covered deal with resource allocations, mechanism design, efficiency and distribution. However, the “currency” for deciding these issues is votes rather than money. Five basic areas of research are covered, all tightly linked to formal theoretical modeling in political science: (1) committee bargaining, (2) elections and candidate competition, (3) voter turnout, (4) information aggregation in committees, and (5) novel voting procedures designed to reflect the intensity of voter preferences. The review of committee bargaining experiments includes early unstructured committee experiments within the framework of cooperative game theory, and more recent sequential bargaining experiments with a fixed extensive form based on noncooperative game theory. The section on elections and candidate competition covers both two-candidate and multicandidate elections, and asymmetric elections in which one candidate (e.g., the incumbent) has a built-in advantage. Voter turnout is modeled as a participation game, intended to rationalize turnout with costly voting in mass elections. The section on information aggregation in committees explores institutions designed to deal with the aggregation of agents’ private information assuming common preferences. Among the issues explored is how the swing voter’s curse (resulting from similar forces as the winner’s curse in common value auctions) is largely corrected for in voting, whereas it is typically not corrected for in auctions. The section on alternative voting mechanisms explores the inefficiency in outcomes when voters have strong cardinal preferences and a number of alternative mechanisms designed to correct these inefficiencies—for example, storable votes and combining voting with markets. Each subsection concludes with a concise summary of results and discussion of open questions to be explored in both theory and experiments.

Chapter 7: “Experimental Economics Across Subject Populations,” by Guillaume R. Fréchette This chapter reviews the results of experiments using nonstandard subjects. In particular, experiments using nonhuman animals, people living in token economies, children, the elderly, demographically varied samples, and professionals are reviewed. Investigating such diverse subject pools addresses the question of the generalizability of findings from the standard undergraduate subject pool, as well as which behaviors are learned and the impact of selection effects and/or experience on experimental outcomes.

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Reasons for why specific subject pools are interesting to study are discussed, along with some of the methodological issues associated with conducting experiments with these different subject pools. The concluding section of the paper pulls these results together with respect to questions of interest in economics. For example, there is reasonably close adherence to GARP (the generalized axiom of revealed preference) across subject populations, which suggests that the behavior is fundamental, and what data there are available for children show that violations decrease with age, so that there is a learned component. For the voluntary contribution mechanism, contributions to the public good respond positively to increases in the marginal per capita return but decline with repetition across both students and nonstudents. The lone exception to this pattern is that young children (less than 12 years of age) do not exhibit decreasing contributions with repetition of the game. With respect to the important question of experiments with professionals versus college students participating in an experiment designed to capture basic elements of professional behavior (e.g., bidding in auctions), he concludes that in most cases results from students carry over, at least qualitatively, to the professionals.

Chapter 8: “Gender,” by Muriel Niederle This chapter reports research exploring gender differences in economic environments. These differences were barely on experimental economists’ radar screen at the time of the first Handbook of Experimental Economics. However, since the turn of the millennium, there has been an explosion of research on gender differences in economics. These have been most extensively studied with respect to attitudes toward competition (with relevance to the glass ceiling effect), altruism and the closely related issue of cooperation, and risk preferences. There are considerable benefits to studying gender differences in the laboratory as this eliminates many of the potential confounds encountered in field settings, which may be particularly important with respect to gender; for example, is the underrepresentation of women in some occupations a result of discrimination (real or anticipated) or a result of different attitudes to highly competitive environments? Results are reported in three main areas: First, with respect to gender difference in risk preferences, the present survey is much more skeptical of consistent differences than earlier surveys, particularly on account of inconsistencies in results across different domains under similar procedures. This survey also notes a lack of economic significance (the small size) of gender differences typically reported. Second, the survey notes that gender differences in altruism tend to be quite mixed, with some studies finding stronger altruism in women, and others not, with what differences there are being relatively small. Third, the survey reports large and consistent differences in reactions to competition between men and women in mixed-gender tournaments, with much smaller differences in outcomes between single-gender tournaments. Experiments exploring the implications of these results for affirmative action in labor markets, along with possible changes in institutional structures (e.g., with respect to education) are explored as well.

Chapter 9: “Auctions: A survey of Experimental Research,” by John H. Kagel and Dan Levin There has been a significant amount of new experimental research on auctions in the last 20 years; much of it motivated by the FCC wireless auctions and the growth of Internet

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auctions. The first part of the chapter revisits some old issues in single-unit private value auctions (e.g., bidding above the risk-neutral Nash equilibrium in first-price private value auctions) as well as how techniques applied to field data can be used both to better explore the experimental data and to better inform some of the assumptions underlying these techniques. Other issues covered include asymmetric and sequential private value auctions, along with new results with respect to second-price private value auctions, including a clever field experiment. The second part of this chapter looks at singleunit common value auction experiments, including auctions with insider information and auctions with an “advantaged bidder” who values the item more than the other bidders, including the role of demographic and ability effects, standard issues in labor economics, on bidders’ ability to overcome the winner’s curse. New experimental results on the winner’s curse in the takeover game, prompted by new theoretical models aimed at better understanding the origin of the winner’s curse, are reported on as well. The last half of the chapter largely covers topics that have gained prominence since publication of the first Handbook. Foremost among these are multiunit-demand auctions in which individual bidders demand multiple items that can be either substitutes or complements due to synergies between items (e.g., regional cell phone licenses that can be combined to provide nationwide coverage). Both theory and experiments here are a direct result of the FCC’s spectrum auctions. Also generating significant attention are experiments focusing on Internet auctions, which have, and continue to be, of growing importance, while also having a variety of interesting institutional characteristics (e.g., a “buy-it-now” price prior to the start of the auction). Experiments in these areas have implications for market design issues covered in Roth (Chapter 5).

Chapter 10: “Learning and the Economics of Small Decisions,” by Ido Erev and Ernan Haruvy This chapter looks at economic outcomes tied to small decisions and whether or not these decisions are reinforced; that is, it looks at economic outcomes determined by indirect shaping processes more familiar to psychologists than economists. Unlike “decisions from description” typical of economic experiments, where the incentive structure is fully laid out, the experiments reported here mostly involve “decisions from experience,” in which decision makers do not receive a prior description of the incentive structure but must learn about it. This results in a number of notable differences from decisions from description. For example, in choice under uncertainty, people exhibit oversensitivity to rare events in decisions from description (as in prospect theory) but exhibit the opposite bias when they need to rely on experience. This “experiencedescription gap” shows up in a number of other settings as well. While many economists might be tempted to dismiss the importance of decisions from experience versus decisions from description, their importance is particularly clear when performance of a task requires a series of small decisions, where the consequences of each decision are relatively small. (The importance of decisions from experience can also be seen from the fact that in most economic experiments, even after attempts at clearly describing the economic contingencies and payoffs, experimental outcomes rarely exhibit equilibrium behavior to begin with, but typically rely on some sort of learning process to move towards equilibrium outcomes.) The practical importance of the economics of small decisions shaped by their consequences is clearly brought out in the concluding section of the paper through examples such as the enforcement of safety

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rules, enhancing the performance of pilots and basketball players, and the implications for financial decision making. We acknowledge with thanks the work of those who contributed chapters or parts of chapters to this edition. John H. Kagel Alvin E. Roth

NOTES 1. There was a conference at Harvard University in 2012, and authors circulated copies of their drafts to specialists in their subfield for comment. 2. The results reported in this chapter, in conjunction with the participation of a number of well-recognized macroeconomic theorists in some of these experiments attests to this. 3. Note, there is considerable overlap, but from a different perspective, in this section and the first part of Cooper and Kagel (Chapter 4) on other-regarding behavior. 4. There is considerable overlap, but from a different perspective, between this part of Cooper and Kagel and Vesterlund (Chapter 2).

THE HANDBOOK OF EXPERIMENTAL ECONOMICS VOLUME 2

1 Macroeconomics: A Survey of Laboratory Research John Duffy

1 INTRODUCTION: LABORATORY MACROECONOMICS Macroeconomic theories have traditionally been tested using nonexperimental field data, most often national income account data on GDP and its components. This practice follows from the widely held belief that macroeconomics is a purely observational science: history comes around just once and there are no “do-overs.” Controlled manipulation of the macroeconomy to gain insight regarding the effects of alternative institutions or policies is viewed by many as impossible, not to mention unethical, and so, apart from the occasional natural experiment, most macroeconomists would argue that macroeconomic questions cannot be addressed using experimental methods.1 Yet, as this survey documents, over the past twenty-five years, a wide variety of macroeconomic models and theories have been examined using controlled laboratory experiments with paid human subjects, and this literature is growing. The use of laboratory methods to address macroeconomic questions has come about in large part due to changes in macroeconomic modeling, though it has also been helped along by changes in the technology for doing laboratory experimentation, especially the use of large computer laboratories. The change in macroeconomic modeling is, of course, the now widespread use of explicit microfounded models of constrained, intertemporal choice in competitive general equilibrium, game-theoretic or searchtheoretic frameworks. The focus of these models is often on how institutional changes or policies affect the choices of decision makers such as household and firms, in addition to the more traditional concern with responses in the aggregate time series data (e.g., GDP) or to the steady states of the model. While macroeconomic models are often expressed at an aggregate level—for instance, there is a “representative” consumer or firm or a market for the “capital good”—an implicit, working assumption of many macroeconomists is that aggregate sectoral behavior is not different from that of the individual actors or components that comprise each sector.2 Otherwise, macroeconomists would be obliged to be explicit about the mechanisms by which individual choices or sectors aggregate up to the macroeconomic representations they work with, and macroeconomists have been largely silent on this issue. Experimentalists testing nonstrategic macroeconomic models

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have sometimes taken this representativeness assumption at face value and conducted individual decision-making experiments with a macroeconomic flavor. But, as we shall see, experimentalists have also considered whether small groups of subjects interacting with one another via markets or by observing or communicating with one another might outperform individuals in tasks that macroeconomic models assign to representative agents. While there is now a large body of macroeconomic experimental research as reviewed in this survey, experimental methods are not yet a mainstream research tool used by the typical macroeconomist, as they are in nearly every other field of economics. This state of affairs likely arises from the training that macroeconomists receive, which does not typically include exposure to laboratory methods and is instead heavily focused on the construction of dynamic stochastic general equilibrium models that may not be well suited to experimental testing. As Sargent (2008, p 27) observes, I suspect that the main reason for fewer experiments in macro than in micro is that the choices confronting artificial agents within even one of the simpler recursive competitive equilibria used in macroeconomics are very complicated relative to the settings with which experimentalists usually confront subjects.

This complexity issue can be overcome, but, as we shall see, it requires experimental designs that simplify macroeconomic environments to their bare essence or involve operational issues such as the specification of the mechanism used to determine equilibrium prices. Despite the complexity issue, I will argue in this survey that experimental methods can and should serve as a complement to the modeling and empirical methods currently used by macroeconomists as laboratory methods can shed light on important questions regarding the empirical relevance of microeconomic foundations, questions of causal inference, equilibrium selection and the role of institutions.3 Indeed, to date the main insights from macroeconomic experiments include (1) an assessment of the microassumptions underlying macroeconomic models, (2) a better understanding of the dynamics of forward-looking expectations, which play a critical role in macroeconomic models, (3) a means of resolving equilibrium selection (coordination) problems in environments with multiple equilibria, (4) validation of macroeconomic model predictions for which the relevant field data are not available, and (5) the impact of various macroeconomic institutions and policy interventions on individual behavior. In addition, laboratory tests of macroeconomic theories have generated new or strengthened existing experimental methodologies, including implementation of the representative-agent assumption, overlapping generations, and searchtheoretic models, methods for assisting with the roles of forecasting and optimizing, implementation of discounting and infinite horizons, methods for assessing equilibration, and the role played by various market clearing mechanisms in characterizing Walrasian competitive equilibrium (for which the precise mechanism of exchange is left unmodeled). The origins of macroeconomic experiments are unclear. Some might point to A. W. Phillips’ (1950) experiments using a colored liquid-filled tubular flow model of the macroeconomy, though this did not involve human subjects! Others might cite Vernon Smith’s (1962) double-auction experiment demonstrating the importance of centralized information to equilibration to competitive equilibrium as the first macroeconomic experiment. Yet another candidate might be John Carlson’s (1967) early experiment examining price expectations in stable and unstable versions of the cobweb model. However, I will place the origins more recently with Lucas’s

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1986 invitation to macroeconomists to conduct laboratory experiments to resolve macrocoordination problems that were unresolved by theory. Lucas’s invitation was followed up on by Aliprantis and Plot (1992), Lim, Prescott, and Sunder (1994), and Marimon and Sunder (1993, 1994, 1995), and, perhaps as the result of their interesting and influential work, over the past two decades, there has been a great blossoming of research testing macroeconomic theories in the laboratory. This literature is now so large that I cannot hope to cover every paper in a single chapter, but I do hope to give the reader a good road map as to the kinds of macroeconomic topics that have been studied experimentally as well as to suggest some further extensions. How shall we define a macroeconomic experiment? One obvious dimension might be to consider the number of subjects in the study. Many might argue that a macroeconomic experiment should involve a large number of subjects; perhaps the skepticism of some toward macroeconomic experiments has to do with the necessarily small numbers of subjects (and small scale of operations) that are possible in laboratory studies.4 The main problem with small numbers of subjects is that strategic considerations may play a role that is not imagined (or possible) in the macroeconomic model that is being tested, which may instead focus on perfectly competitive Walrasian equilibrium outcomes. However, research has shown that attainment of competitive equilibrium outcomes might not require large numbers of subjects. For example, the evidence from numerous double-auction experiments beginning with Smith (1962) and continuing to the present reveals that equilibration to competitive equilibrium can occur reliably with as few as three to five buyers or sellers on each side of the market. Duffy and others (2011) study bidding behavior in a Shapley-Shubik market game and show that with small numbers of subjects (e.g., groups of size two), Nash equilibrium outcomes are indeed far away from the competitive equilibrium outcome of the associated pure exchange economy. However, they also show that as the number of subjects increases, the Nash equilibrium subjects coordinate upon becomes approximately Walrasian; economies with just ten subjects yield market-based allocations that are indistinguishable from the competitive equilibrium of the associated pure exchange economy. Thus, while more subjects are generally better than fewer subjects for obtaining competitive equilibrium outcomes, it seems possible to establish competitive market conditions with the small numbers of subjects available in the laboratory.5 A more sensible approach is to define a macroeconomic experiment as one that tests the predictions of a macroeconomic model or its assumptions or is framed in the language of macroeconomics, involving, for example, intertemporal consumption and savings decisions, inflation and unemployment, economic growth, bank runs, monetary exchange, monetary or fiscal policy, or any other macroeconomic phenomena. Unlike microeconomic models and games, which often strive for generality, macroeconomic models are typically built with a specific macroeconomic story in mind that is not as easily generalized to other nonmacroeconomic settings. For this reason, our definition of a macroeconomic experiment may be too restrictive. There are many microeconomic experiments—coordination games for instance—that can be given both a macroeconomic interpretation or a more microeconomic interpretation, for example; as models of firm or team behavior. In discussing those studies as macroeconomic experiments, I will attempt to emphasize the macroeconomic interpretation. The coverage of this chapter can be viewed as an update on some topics covered in several chapters of the first volume of the Handbook of Experimental Economics, including discussions of intertemporal decision making by Camerer (1995), coordination problems by Ochs (1995), and asset prices by Sunder (1995), though the coverage

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here will not be restricted to these topics alone. Most of the literature surveyed here was published since 1995, the date of the first Handbook volume. In addition, this chapter builds on, complements, and extends earlier surveys of the macroeconomic experimental literature by myself, Duffy (1998, 2008), and by Ricciuti (2008).

2 DYNAMIC, INTERTEMPORAL OPTIMIZATION Perhaps the most widely used model in modern macroeconomic theory is the onesector, infinite-horizon optimal-growth model pioneered by Ramsey (1928) and further developed by Cass (1965) and Koopmans (1965). This model posits that individuals solve a dynamic, intertemporal optimization problem in deriving their consumption and savings plan over an infinite horizon. Both deterministic and stochastic versions of this model are workhorses of modern real business cycle theory and growth theory. In the urge to provide microfoundations for macroeconomic behavior, modern macroeconomists assert that the behavior of consumers or firms can be reduced to that of a representative, fully rational individual actor; there is no room for any “fallacies of composition” in this framework. It is, therefore, of interest to assess the extent to which macroeconomic phenomena can be said to reflect the choices of individuals facing dynamic stochastic intertemporal optimization problems. Macroeconomists have generally ignored the plausibility of this choice-theoretic assumption, preferring instead to examine the degree to which the time-series data on GDP and its components move in accordance with the conditions that have been optimally derived from the fully rational representative-agent model and especially whether these data react predictably to shocks or policy interventions. 2.1 Optimal Consumption/Savings Decisions Whether individuals can in fact solve a dynamic stochastic intertemporal optimization problem of the type used in the one-sector optimal growth framework has been the subject of a number of laboratory studies, including Hey and Dardanoni (1988), Carbone and Hey (2004), Noussair and Matheny (2000), Lei and Noussair (2002), Ballinger, Palumbo, and Wilcox (2003), Carbone (2006), Brown, Chua, and Camerer (2009), Ballinger and others (2011), Crockett and Duffy (2013), Carbone and Duffy (2014), and Meissner (2016), among others. These studies take the representative agent assumption of modern macroeconomics seriously and ask whether subjects can solve a discrete-time optimization problem of the form max E t {c t }

subject to

∞ 

β t u(c t )

t=0

c t + xt ≤ ωt

where c t is time t consumption, u(·) is a concave utility function, β is the period discount factor, xt represents time t savings (if positive) or borrowings (if negative), and ωt is the household’s time t wealth. Hey and Dardanoni (1988) assume a pure exchange economy, where wealth evolves according to ωt = R(ωt−1 − c t−1 ) + yt , with ω0 > 0 given. Here, R denotes the (constant) gross return on savings and yt is the stochastic time t endowment of the single

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good; the mean and variance of the stochastic income process is made known to subjects. By contrast, Noussair and associates assume a nonstochastic production economy, where ωt = f (kt ) + (1 − δ)kt , with f (·) representing the known, concave production function, kt denoting capital per capita, and δ denoting the depreciation rate. In this framework, it is public knowledge that an individual’s savings, xt , are invested in capital and become the next period’s capital stock, that is, xt = kt+1 . The dynamic law of motion for the production economy is expressed in terms of capital rather than wealth: kt+1 = f (kt ) + (1 − δ)kt − c t , with k0 > 0 given. The gross return on savings is endogenously determined by R = f  (kt ) + (1 − δ). Solving the maximization problem given before, the first-order conditions imply that the optimal consumption program must satisfy the Euler equation u (c t ) = β R E t u (c t+1 ) where the expectation operator is with respect to the (known) stochastic process for income (or wealth). Notice that the Euler equation predicts a monotonic increasing, decreasing, or constant consumption sequence, depending on whether β R is less than, greater than, or equal to 1. Solving for a consumption or savings function involves application of dynamic programming techniques that break the optimization problem up into a sequence of two-period problems; the Euler equation characterizes the dynamics of marginal utility in any two periods. For most specifications of preferences, analytic closed-form solutions for the optimal consumption or savings function are not possible, though via concavity assumptions, the optimal consumption/savings program can be shown to be unique. In testing this framework, Hey and Dardanoni (1988) addressed several implementation issues. First, they chose to rule out borrowing (negative saving) in order to prevent subjects from ending the session in debt. Second, they attempted to implement discounting and the stationarity associated with an infinite horizon by having a constant probability that the experimental session would continue with another period.6 Finally, rather than inducing a utility function, they supposed that all subjects had constant absolute risk-aversion preferences, and they estimated each individual subject’s coefficient of absolute risk aversion using data they gathered from hypothetical and paid choice questions presented to the subjects. Given this estimated utility function, they then numerically computed optimal consumption for each subject and compared it with their actual consumption choice. To challenge the theory, they considered different values for R and β as well as for the parameters governing the stochastic income process, y. They report mixed results. First, consumption is significantly different from optimal behavior. In particular, there appears to be great time dependence in consumption behavior; that is, consumption appears dependent on past income realizations, which is at odds with the time-independent nature of the optimal consumption program. Second, they find support for the comparative statics implications of the theory. That is, changes in the discount factor, β, or in the return on savings, R, have the same effect on consumption as under optimal consumption behavior. So they find mixed support for dynamic intertemporal optimization. Carbone and Hey (2004) and Carbone (2006) simplify the design of Hey and Dardanoni. First, they eliminate discounting and consider a finite-horizon, twenty-five period model. They argue, based on the work of Hey and Dardanoni, that subjects “misunderstand the stationarity property” of having a constant probabilistic stopping rule. Second, they greatly simplify the stochastic income process, allowing there to be

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Chapter 1 TABLE 1.1: Average change in consumption in response to parameter changes and conditional on employment status. Source: Carbone and Hey (2004, Table 5). Change () in Treatment Variable (from low value to high value) p (Pr. remaining employed) q (Pr. becoming employed)  Ratio high-low income

Unemployed Optimal Actual 5.03 14.73 0.25

23.64 −1.08 0.24

Employed Optimal Actual 14.57 5.68 0.43

39.89 0.15 0.76

just two values for income—one high, which they refer to as a state where the consumer is “employed,” and the other low, in which state the consumer is “unemployed.” They use a two-state Markov process to model the state transition process: conditional on being employed (unemployed), the probability of remaining (becoming) employed was p(q), and these probabilities were made known to subjects. Third, rather than infer preferences they induce a constant absolute risk-aversion utility function. Their treatment variables were p, q, R and the ratio of employed to unemployed income; they considered two values of each, one high and one low, and examined how consumption changed in response to changes in these treatment variables relative to the changes predicted by the optimal consumption function (again numerically computed). Table 1.1, shows a few of their comparative statics findings. An increase in the probability of remaining employed caused subjects to overreact in their choice of additional consumption relative to the optimal change regardless of their employment status (unemployed or employed), whereas an increase in the probability of becoming employed—a decrease in the probability of remaining unemployed—led to an underreaction in the amount of additional consumption chosen relative to the optimal prediction. On the other hand, the effect of a change in the ratio of high-to-low income on the change in consumption was quite close to optimal. Carbone and Hey emphasize also that there was tremendous heterogeneity in subjects’ abilities to confront the lifecycle consumption savings problem, with most subjects appearing to discount old-age consumption too heavily (when they should not discount at all) or optimizing over a shorter planning horizon than the twenty-five periods of the experiment.7 Carbone and Hey conclude that “subjects do not seem to be able to smooth their consumption stream sufficiently—with current consumption too closely tracking current income.” Interestingly, the excess sensitivity of consumption to current income (in excess of that warranted by a revision in expectations of future income) is a well-documented empirical phenomenon in studies of consumption behavior using aggregate field data (see, e.g., Flavin 1981; Hayashi 1982; Zeldes 1989). This corroboration of evidence from the field should give us further confidence in the empirical relevance of the laboratory analyses of intertemporal consumption-savings decisions. Two explanations for the excess sensitivity of consumption to income that have appeared in the literature are (1) binding liquidity constraints and (2) the presence of a precautionary savings motive (which is more likely in a finite-horizon model). Future experimental research might explore the relative impacts of these two factors on consumption decisions. Meissner (2016) modifies the finite-horizon, life-cycle planning environment of Carbone and Hey (2004) to allow subjects to borrow and not just to save. In particular, Meissner studies two regimes, one in which an individual’s stochastic income process has an upward-sloping trend and a second regime where this income process has a

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downward-sloping trend. Optimal behavior in the first regime involves borrowing in the early periods of life so as to better smooth consumption, while optimal behavior in the second regime involves saving in the early periods of life to better smooth consumption. Meissner parameterized the environment so that the optimal consumption path was the same in both income treatments, and subjects were given three opportunities or “lifetimes” to make consumption/savings/borrowing decisions in each of the two income treatments, that is, he uses a within-subjects design. A main finding is that in the decreasing-income regime, subjects have no trouble learning to save in the early periods of their life and can approximately smooth consumption over their lifetime. By contrast, in the increasing-income regime, most subjects seem averse to borrowing any amount, so that consumption deviates much further from the optimal path; consumption decisions in this treatment more closely track the upward-trend path of income and there is not much difference with replication (i.e., there is little learning). Meissner attributes the latter finding to “debt aversion” on the part of his university student subjects. It would be of interest to explore whether such debt aversion continues in more-general subject populations involving individuals who may have some homegrown experience with acquiring debt. Noussair and Matheny (2000) further modify the framework of Hey and associates by adding a concave production technology, f (kt ) = Aktα , α < 1, which serves to endogenize the return on savings in conformity with modern growth theory. They induce both the production function and a logarithmic utility function by giving subjects schedules of payoff values for various levels of k and c, and they implement an infinite horizon by having a constant probability that a sequence of rounds continues. Subjects made savings decisions (chose xt = kt+1 ) with the residual from their budget constraint representing their consumption. Noussair and Matheny varied two model parameters, the initial capital stock k0 and the production function parameter α. Variation in the first parameter changes the direction by which paths for consumption and capital converge to steady-state-values (from above or below) while variations in the second parameter affect the predicted speed of convergence; the lower is α, the greater is the speed of convergence of the capital stock and consumption to the steady state of the model. Among the main findings, Noussair and Matheny report that sequences for the capital stock are monotonically decreasing regardless of parameter conditions, and theoretical predictions with regard to speed of convergence do not find much support. Consumption is, of course linked to investment decisions and is highly variable. They report that subjects occasionally resorted to consumption binges, allocating nearly nothing to the next period’s capital stock in contrast to the prediction of consumption smoothing. However, this behavior seemed to lessen with experience. A virtue of the Noussair-Matheny study is that it was conducted with both US and Japanese subjects, with similar findings for both countries. One explanation for the observed departure of behavior from the dynamically optimal path is that the representative-agent assumption, while consistent with the reductionist view of modern macroeconomics, assumes too much individual rationality to be useful in practice.8 Information on market variables (e.g., prices) as determined by many different interacting agents, may be a necessary aid to solving such complicated optimization decisions. An alternative explanation may be that the standard model of intertemporal consumption smoothing abstracts away from the importance of social norms of behavior with regard to consumption decisions. Akerlof (2007), for instance, suggests that people’s consumption decisions may simply reflect their “station in life.” College students (the subjects in most of these experiments) looking to their peers,

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choose to live like college students with expenditures closely tracking income. Both of these alternative explanations have been considered to some extent in further laboratory studies. Crockett and Duffy (2013) explore whether groups of subjects can learn to intertemporally smooth their consumption in the context of an infinite-horizon, consumptionbased asset-pricing model, specifically, the Lucas tree model (Lucas 1978). In the environment they study, the only means of saving intertemporally is to buy or sell shares of a long-lived asset (a Lucas tree), which yields a known and constant divided (amount of fruit) each period. Subjects are of two types, according to the endowment of income they receive in alternating periods; odd types receive high income in odd-numbered periods and low income in even-numbered periods, while even types receive high income in even-numbered periods and low income in odd-numbered periods. In one of Crockett and Duffy’s treatments, subjects’ induced utility function over consumption is concave so that subjects have an incentive to intertemporally smooth their consumption by buying the asset in their high-income periods and selling it in their low-income periods (the heterogeneity of subject types allows for such trades to occur). Asset prices are determined via a double-auction mechanism, and these prices can be observed by all subject participants. Crockett and Duffy report that with these asset price signals, most subjects have little difficulty learning to intertemporally smooth their consumption across high- and low-income periods. Future experimental research on consumption smoothing through the purchase and sale of long-lived assets might investigate a more realistic, stochastic, life-cycle income process. Ballinger, Palumbo, and Wilcox (2003) explore the role of social learning in a modified version of the noisy pure exchange economy studied by Hey and Dardanoni (1988). In particular, they eliminate discounting (presumably to get rid of time dependence), focusing on a finite sixty-period horizon. Subjects are matched into three-person “families” and make decisions in a fixed sequence. The generation 1 (G1) subject makes consumption decisions alone for twenty periods; in the next twenty periods (21–40), his or her behavior is observed by the generation 2 (G2) subject, and in one treatment, the two are free to communicate with one another. In the next twenty periods (periods 41– 60 for G1, periods 1–20 for G2), both generations make consumption/savings decisions. The G1 subject then exits the experiment. The same procedure is then repeated with the generation 3 (G3) subject watching the G2 subject for the next twenty rounds, and so on. Unlike Hey and Dardanoni, Ballinger and others induce a constant relative risk-aversion utility function on subjects using a Roth and Malouf (1979) binary lottery procedure. This allows them to compute the path of optimal consumption/savings behavior. These preferences give rise to a precautionary savings motive, wherein liquid wealth (saving) follows a hump-shaped pattern over the sixty-period lifecycle. Ballinger, Palumbo, and Wilcox’s (2003) main treatment variable concerns the variance of the stochastic income process (high or low), which affects the peak of the precautionary savings hump; in the high case they also explore the role of allowing communication/mentoring or not (while maintaining observability of actions by overlapping cohorts at all times). Among their findings, they report that subjects tend to consume more than the optimal level in the early periods of their lives, leading to less savings and below-optimal consumption in the later periods of life. However, savings are greater in the high- as compared with the low-variance case, which is consistent with the comparative statics prediction of the rational intertemporal choice framework. They also find evidence for time dependence in that consumption behavior is excessively sensitive to near lagged changes in income. Most interestingly,

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they report that consumption behavior of generation 3 is significantly closer to the optimal consumption program than in the consumption behavior of generation 1, suggesting that social learning by observation plays an important role and may be a more reasonable characterization of the representative agent. Ballinger and others (2011) study a similar life-cycle consumption/savings problem but focus on whether cognitive and/or personality measures might account for the observed heterogeneity in a subject’s savings behavior, in particular, the subject’s use of shorter-than-optimal planning horizons. Using a careful multivariate regression analysis that accounts for potentially confounding demographic variables, they report that cognitive measures and not personality measures are good predictors of heterogeneity in savings behavior. In particular, they report that variations in subjects’ cognitive abilities, as assessed, using visually oriented “pattern-completion” tests and “working memory” tests that assess a subject’s ability to control both attention and thought, can explain variations in a subject’s life-cycle savings behavior and that the median subject is thinking just three periods ahead. Lei and Noussair (2002) study the intertemporal consumption savings problem in the context of the one-sector optimal growth model with productive capital. They contrast the “social planner” case, where a single subject is charged with maximizing the representative consumer firms’ present discounted sum of utility from consumption over an indefinite horizon (as in Noussair and Matheny (2000)), with a decentralized market approach, wherein the same problem is solved by five subjects looking at price information. In this market treatment, the production and utility functions faced by the social planner are disaggregated into five individual functions assigned to the five subjects that aggregate up to the same functions faced by the social planner. For example, some subjects had production functions with marginal products for capital that were higher than for the economy-wide production function, while others had marginal products for capital that are lower. At the beginning of a period, production took place, based on previous period’s capital, using either the individual production functions in the market treatment or the economy-wide production function in the social-planner treatment. Next, in the market treatment, a double-auction market for output (or potential future capital) opened up. Agents with low marginal products of capital could trade some of their output to agents with high marginal products for capital in exchange for experimental currency units (subjects were given an endowment of such units each period, which they had to repay). The import of this design was that the market effectively communicated to the five subjects the market price of a unit of output (or future capital). As future capital could be substituted one for one with future consumption, the market price of capital revealed to subjects the marginal utility of consumption. After the market for output closed, subjects in the market treatment could individually allocate their adjusted output levels between future capital kt+1 or savings and experimental currency units or consumption c t . By contrast, in the social-planner treatment, there was no market for output; the representative individual proceeded directly to the step of deciding how to allocate output between future capital (savings) and current consumption. At the end of the period, subjects’ consumption amounts were converted into payoffs using the economy-wide or individual concave utility functions, and loans of experimental currency units in the market treatment were repaid. The difference in consumption behavior between the market and representativeagent–social planner treatments is illustrated in Figure 1.1, which shows results from a representative session of one of Lei and Noussair’s treatments. In the market treatment,

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there was a strong tendency for consumption (as well as capital and the price of output) to converge to their unique steady-state values, while in the social planner treatment, consumption was typically below the steady-state level and much more volatile. In further analysis, Lei and Noussair (2002) make use of a linear, panel dataregression model to assess the extent to which consumption and savings (or any other time-series variable for that matter) can be said to be converging over time toward predicted (optimal) levels.9 In this regression model, y j,t denotes the average (or economy-wide level) of the variable of interest by cohort/session j in period t = 1, 2, . . ., and D j is a dummy variable for each of the j = 1, 2, . . . , J cohorts. The regression model is written as y j,t = α1

D1 D2 DJ t −1 + α2 · · · + αJ +β +  j,t t t t t

(1)

where  j,t is a mean zero, random error term. The α j coefficients capture the initial starting values for each cohort, while the β coefficient captures the asymptotic value of the variable y to which all J cohorts of subjects are converging; notice that the α coefficients have a full weight of 1 in the initial period 1 and then have exponentially declining weights, while the single β coefficient has an initial weight of zero that increases asymptotically to 1. For the dependent variable in (1), Lei and Noussair (2002) use: (1) the consumption and capital stocks (savings) of cohort j , c j,t , and k j,t+1 , (2) the absolute deviation of consumption from its optimal steady-state value, |c j,t − c ∗ |, and (3) the ratio of the realized utility of consumption to the optimum, u(c j,t )/u(c ∗ ). For the first type of dependent variable, the estimate βˆ reveals the values to which the dependent

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variable, c j,t and k j,t are converging across cohorts; strong convergence is said to obtain if βˆ is not significantly different from the optimal steady-state levels, c ∗ and k ∗ . For the second and third types of dependent variable, one looks for whether βˆ is significantly different from zero or one, respectively. Lei and Noussair also consider a weaker form of convergence that examines whether βˆ is closer (in absolute value) to the optimal, predicted level than a majority of the αˆ j estimates. Using all four dependent variables, they report evidence of both weak and strong convergence in the market treatment, but only evidence of weak (and not strong) convergence in the social planner treatment.10 Tests of convergence based on the regression model (1) can be found in several experimental macroeconomic papers reviewed later in this chapter. This methodology for assessing convergence of experimental time series is one of several methodologies that might be considered “native” to experimental macroeconomics. Therefore, allow me a brief digression on the merits of this approach. First, the notion that strong convergence obtains if βˆ is not significantly different from the predicted level, y ∗ , while weak convergence obtains if |βˆ − y ∗ | < |αˆ j − y ∗ | for a majority of j s is somewhat problematic, as strong convergence need not imply weak convergence, as when the αˆ j ˆ Second, if convergence is truly the focus, estimates are insignificantly different from β. an alternative approach would be to use an explicitly dynamic adjustment model for each cohort j of the form y j,t = λ j y j,t−1 + μ j +  j,t

(2)

Using (2), weak convergence would obtain if the estimates, λˆ j , were significantly less than 1, while strong convergence would obtain if the estimate of the long-run expected ˆ j /(1 − λˆ j ), was not significantly different from the steady-state prediction value for y j , μ ∗ y ; in this model, strong convergence implies weak convergence, not the reverse.11 Finally, analysis of joint convergence across the J cohorts to the predicted level y ∗ could be studied through tests of the hypothesis: ⎛ ∗⎞ ⎞ ⎛ ⎞ y μ ˆ1 λˆ 1 ⎜ .. ⎟ ⎜ .. ⎟ ∗ ⎜ .. ⎟ IJ ⎝ . ⎠ + ⎝ . ⎠ y = ⎝ . ⎠ μ ˆJ y∗ λˆ J ⎛

where I J is a J -dimensional identity matrix. Returning to the subject of dynamic, intertemporal life-cycle consumption/savings decisions, recent work has explored subject behavior in the case where there are two (as opposed to just one) state variables: an individual’s wealth (or “cash on hand” ) ωt and some induced “habit” level for consumption h t (following the macroeconomic literature on habit formation), so that the period objective function is of the form u(c t , h t ). Brown, Chua, and Camerer (2009) study the case of internal habit formation, where each individual subject i has his or her own, personal habit level of consumption that evolves according to h it = αh it−1 + c ti (α < 1) and has a period utility function that is increasing in the ratio of c ti / h it . Carbone and Duffy (2014) study the case of external habit formation, where h t is the lagged average consumption of a group of N i ) and u is an increasing function identically endowed subjects (i.e., h t = N −1 iN=1 c t−1 of the difference, c t − αh t (α < 1). Both studies also explore social learning in this more complex environment, with Brown and others exploring intergenerational learning and

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Carbone and Duffy exploring peer-to-peer social learning. Both studies report that subjects have some difficulty with habit-formation specifications as they require that subjects optimally save more early on in their life-cycle (relative to the absence of a habit variable) to adjust for the diminishing effect that habits have on utility over the lifecycle, and consistent with earlier studies (without habit), consumers typically undersave early on in their life-cycle. Brown and others find that information on the lifecycle consumption/savings choices made by prior experienced generations of subjects (intergenerational learning) improves the performance of subsequent generations of subjects (in terms of closeness to the optimal path). However Carbone and Duffy report that social information on the contemporary consumption/savings choices of similarly situated peers (peer-to-peer learning) does not improve performance in the model with (or without) habit in the utility function. Future experimental research on dynamic, intertemporal consumption/savings plans might explore the impact of other realistic but currently missing features, such as mortality risk, an active borrowing and lending market among agents of different ages, consumption/leisure trade-offs, and the consequences of retirement and social security systems. 2.2 Exponential Discounting and Infinite Horizons It is common in macroeconomic models to assume infinite horizons, as the representative household is typically viewed as a dynasty, with an operational bequest motive linking one generation with the next. Of course, infinite horizons are not operational in the laboratory, but indefinite horizons are. As we have seen, in experimental studies, these have often been implemented by having a constant probability δ that a sequence of decision rounds continues with another round.12 Theoretically this practice should induce both exponential discounting of future payoffs at rate δ per round as well as the stationarity associated with an infinite horizon, in the sense that, for any round reached, the expected number of future rounds to be played is always δ + δ 2 + δ 3 + . . . , or, in the limit δ/(1 − δ). Empirically, there is laboratory evidence that suggests that probabilistic continuation does affect subjects’ perceptions of short-run versus long-run incentives as predicted by theory. For instance, Dal Bó (2005) reports lower cooperation for finiteduration experiments in comparison to indefinite-duration experiments having the same expected length. In particular, Dal Bó reports that aggregate cooperation rates are positively correlated with the continuation probability implemented. To better induce discounting at rate δ, it seems desirable to have subjects participate in several indefinitely repeated sequences of rounds within a given session—as opposed to a single indefinitely repeated sequence—as the former practice provides subjects with the experience that a sequence ends and thus a better sense of the intertemporal rate of discount they should apply to payoffs. A further good practice is to make transparent the randomization device for determining whether an indefinite sequence continues or not, for example, by letting the subjects themselves roll a die at the end of each round using a rolling cup. A difficult issue is the possibility that an indefinite sequence continues beyond the scheduled time of an experimental session. One approach to dealing with this problem is to recruit subjects for a longer period of time than is likely necessary, say, several hours, and inform them that a number of indefinitely repeated sequences of rounds will be played for a set amount of time—say for one hour following the reading of instructions. Subjects would be further instructed at the outset of the session that after that set amount of time had passed, the indefinite sequence of rounds currently in

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play would be the last indefinite sequence of the experimental session. In the event that this last indefinite sequence continued beyond the long period scheduled for the session, subjects would be instructed that they would have to return at a later date and time that was convenient for everyone to complete that final indefinite sequence. In practice, as we have seen, some researchers feel more comfortable working with finite-horizon models. However, replacing an infinite horizon with a finite horizon may not be innocuous; such a change may greatly alter predicted behavior relative to the infinite-horizon case. For instance, the finite-horizon life-cycle model of the consumption-savings decision greatly increases the extent of the precautionary savings motive relative to the infinite-horizon case. Other researchers have chosen not to tell subjects when a sequence of decision rounds is to end (e.g., Offerman et al. 2001), or to exclude data from the end rounds (e.g., Ule et al. 2009) as a means of gathering data from an approximately infinite horizon. A difficulty with that practice is that the experimenter loses control of subjects’ expectations regarding the likely continuation of a sequence of decisions and appropriate discounting of payoffs. This can be a problem if, for instance, the existence of equilibria depend on the discount factor being sufficiently high. Yet another approach is to exponentially discount the payoffs that subjects receive in each round but at some point in the session switch over to a stochastic termination rule (e.g., Feinberg and Husted 1993). A problem with this approach is that it does not implement the stationarity associated with an infinite horizon. 2.3 Exponential or Hyperbolic Discounting? Recently, there has been a revival of interest in time-inconsistent preferences with regard to consumption-savings decisions, where exponential discounting is replaced by a quasi-hyperbolic form so that the representative agent is viewed as maximizing u(c t ) + β

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where δ ∈ (0, 1) is a discount factor and the parameter β ≤ 1 characterizes the agent’s bias for the present (exponential discounting has β = 1).13 Agents who discount hyperbolically (β < 1) rather than exponentially may exhibit time-inconsistent behavior (self-control problems) in that they systematically prefer to reverse earlier decisions, for example, regarding how much they have saved. Thus, a possible explanation for the departures from optimal consumption paths noted before in experimental studies of intertemporal decision making may be that subjects have such present-biased preferences. Indeed, Laibson (1997), O’Donoghue and Rabin (1999), and several others have shown that consumers with such preferences save less than exponential consumers. Although time-inconsistent preferences have been documented in numerous psychological studies (see, e.g., Frederick, Loewenstein, and O’Donoghue (2002) for a survey) the methodology used has often consisted of showing inconsistencies in hypothetical (i.e., unpaid) money-time choices (e.g., Thaler 1981). For example, subjects are asked whether they would prefer $D now or $D(1 + r ) t periods from now, where variations in both r and t are used to infer individual rates of time preference. Recently, nonhypothetical (i.e., paid) money-time choice experiments have been conducted that more carefully respect the time dimension of the trade-off (e.g., Coller, Harrison, and Rutström (2005); Benhabib, Bisin, and Schotter (2010). These studies cast doubt on the notion that discounting is consistent with either exponential or quasi-hyperbolic

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models of discounting. For instance, Benhabib and others report that discount rates appear to vary with both the time delay from the present and the amount of future rewards in contrast to exponential discounting. However, Coller and others show that in choices between money rewards to be received only in the future, for example, seven days from now versus thirty days from now, variations in the time delay between such future rewards do not appear to affect discount rates, which is consistent with both exponential and quasi-hyperbolic discounting but inconsistent with continuous hyperbolic discounting. Consistent with quasi-hyperbolic discounting both studies find that a small fixed premium attached to immediate versus delayed rewards, can reconcile much of the variation in discount rates between the present and the future and between different future rewards. However, this small fixed premium does not appear to vary with the amount of future rewards (Benhabib et al.) and may simply reflect transaction/credibility costs associated with receiving delayed rewards (Coller et al.), making it difficult to conclude definitively in favor of the quasi-hyperbolic model. Anderson et al. (2008) make a strong case that time preferences cannot be elicited apart from risk preferences. Prior studies on time discounting all presume that subjects have risk-neutral preferences. However, if subjects have risk-averse preferences (concave utility functions) as is typically the case, the implied discount rates from the binary time-preference choices will be lower than under the presumption of risk neutrality (linear utility functions). Indeed, Anderson et al. (2008) elicit joint time and risk preferences by having each subject complete sequences of binary lottery choices (of the Holt and Laury (2002) variety) that are designed to elicit risk preferences as well as sequences of binary time-preference choices that are designed to elicit their discount rates (similar to those in the Coller et al. study). They find that once the risk aversion of individual subjects is taken into account, the implied discount rates are much lower than under the assumption of risk-neutral preferences. This finding holds regardless of whether discounting is specified to be exponential or quasi-hyperbolic or some mixture. Of course, one must use caution in extrapolating from experimental findings on intertemporal decision making to the intertemporal choices made by the representative household, firm, government agencies, or institutions in the macroeconomy. Internal, unaccounted-for factors may bias intertemporal decision making in ways that experimental evidence cannot easily address; for example, election cycles or other seasonal factors may influence decision making in ways that would be difficult to capture in a laboratory setting. 2.4 Expectation Formation In modern, self-referential macroeconomic models, expectations of future endogenous variables play a critical role in the determination of the current values of those endogenous variables; that is, beliefs affect outcomes, which in turn affect beliefs, which affect outcomes, and so on. Since Lucas (1972) it has become standard practice to assume that agents’ expectations are rational in the sense of Muth (1961), and indeed most models are “closed” under the rational expectations assumption. The use of rational expectations to close self-referential models means that econometric tests of these models using field data are joint tests of the model and the rational expectations assumption, confounding the issue of whether the expectational assumption or other aspects of the model are at fault if the econometric evidence is at odds with theoretical predictions. While many tests of rational expectations have been conducted using survey data, (e.g. Frankel and Froot 1987), these tests are beset by problems of interpretation,

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for example, due to uncontrolled variations in underlying fundamental factors, or to the limited incentives of forecasters to provide accurate forecasts, or to disagreement about the true underlying model or data-generating process. By contrast, in the lab it is possible to exert more control over such confounding factors, to know for certain the true data-generating process, and to implement the self-referential aspect of macroeconomic models. Early experimental tests of rational expectations involved analyses of subjects’ forecasts of exogenous, stochastic processes for prices, severing the critical self-referential aspect of macroeconomic models but controlling for the potentially confounding effects of changes in fundamental factors (e.g., Schmalensee 1976; Dwyer et al. (1993). Later experimental tests involved elicitation of price forecasts from subjects who were simultaneously participants in experimental asset markets that were determining the prices being forecast (Williams 1987; Smith, Suchanek, and Williams (1988). As discussed in the prior handbook surveys by Camerer (1995) and Ochs (1995), many (though not all) of these papers found little support for rational expectations in that forecast errors tended to have nonzero means and were autocorrelated or were correlated with other observables. Further, the path of prices sometimes departed significantly from rational expectations equilibrium. However, most of these experimental studies involve analyses of price forecasts in environments where there is no explicit mechanism by which forecasts determine subsequent outcomes, as is assumed in forward–looking macroeconomic models. Further, some of these experimental tests (e.g., Smith et al.) involved analyses of price forecasts for relatively short periods of time or in empirically nonstationary environments where trading behavior resulted in price bubbles and crashes, providing a particularly challenging test for rational expectations hypothesis. Marimon and Sunder (1993, 1994) recognized the challenge to subjects of both forecasting prices and then using those forecasts to solve complicated dynamic optimization problems. They pioneered an approach that has come to be known as a learning-to-forecast experimental design, another methodology that might be considered “native” to experimental macroeconomics. In their implementation, subjects were asked each period to form inflationary expectations in a stationary overlappinggenerations economy. These forecasts were then used as input into a computer program that solved for each individual’s optimal, intertemporal consumption/savings decision given that individual’s forecast. Finally, via market clearing, the actual price level was determined and therefore the inflation rate. Subjects were rewarded only for the accuracy of their inflation forecasts and not on the basis of their consumption/savings decision, which was, after all, chosen for them by the computer program. Indeed, subjects were not even aware of the underlying overlapping-generations model in which they were operating—instead they were engaged in a simple forecasting game. This learning-to-forecast approach may be contrasted with a “learning-to-optimize” experimental design, wherein subjects are simply called upon to make choice decisions (e.g. consumption/savings) having intertemporal consequences but without elicitation of their forecasts (which are implicit). This is an interesting way of decomposing the problem faced by agents in complex macroeconomic settings so that it does not involve a joint test of rationality in both optimization and expectation formation; indeed, the learning to forecast experimental design has become a workhorse approach in experimental macroeconomics—see Hommes (2011) for a comprehensive survey. More recently some macroeconomists have come to believe that rational expectations presumes too much knowledge on the part of the agents who reside within these models. For instance, rational expectations presumes common knowledge of

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rationality. Further, rational expectations agents know with certainty the underlying model, whereas econometricians are often uncertain of data-generating processes and resort to specification tests. Given these strong assumptions, some researchers have chosen to replace rational expectations with some notion of bounded rationality and ask whether boundedly rational agents operating for some length of time in a known, stationary environment might eventually learn to possess rational expectations from observation of the relevant time-series data (see, e.g., Sargent (1993, 1999) and Evans and Honkapohja (2001) for surveys of the theoretical literature). Learning to forecast experiments have played a complementary role to the literature on learning in macroeconomic systems. This literature imagines that agents are boundedly rational in the sense that they do not initially know the model (data-generating process) and behave more as econometricians, using possibly misspecified model specifications for their forecasting rules, which they update in real time as new data become available. In addition to the work of Marimon and Sunder (1993, 1994), this real-time, adaptive expectations approach has been explored experimentally using the learning to forecast design by Bernasconi, Kirchkamp, and Paruolo (2006), Hey (1994), Van Huyck Cook, and Battalio (1994), Kelley and Friedman (2002), Hommes and others (2005, 2007), Heemeijer and others (2009), and Bao and others (2012), Bao, Duffy, and Hommes (2013). The use of the learning to forecast methodology has become particularly important in assessing policy predictions using the expectations-based New Keynesian model of the monetary-transmission mechanism in experimental studies by Adam (2007), Pfajfar and Zakelj (2015), Assenza and others (2013), and Petersen (2015), as will be discussed in Section 5.3. Hommes and others (2007) provide a good representative example of this literature. They consider expectation formation by groups of six subjects operating for a long time (in the laboratory sense)—fifty periods—in the simplest dynamic and self-referential model, the cobweb model.14 In each of the fifty periods, all six subjects are asked to e , using all supply a one-step-ahead forecast of the price that will prevail at time t, pi,t available past price data through time t − 1; the forecast is restricted to lie in the interval (0, 10). These price forecasts are automatically converted into supply of the single good e e ; λ), which is increasing in pi,t and has common parameter via a supply function s ( pi,t λ governing the nonlinearity of the supply function. Demand is exogenous and given by a linear function D( pt ). The unique equilibrium price p ∗ is thus given by pt∗ = D −1

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that is, it is completely determined by subjects’ price forecasts. However, Hommes and others add a small shock to exogenous demand, which implies that prices should evolve according to pt = pt∗ + , where  ∼ N(0, σ2 ). Thus, under rational expectations, all forecasters should forecast the same price, p ∗ . In the new learning view of rational expectations, it is sufficient that agents have access to the entire past history of prices for learning of the rational-expectations solution to take place. Consistent with this view, Hommes and others do not inform subjects of the market clearing process by which prices are determined. Instead, subjects are simply engaged in forming accurate price forecasts and individual payoffs are a linearly decreasing function of the quadratic loss e 2 ) . The main treatment variable consists of variation in the supply function ( pt − pi,t parameter λ, which affects the stability of the cobweb model under the assumption

Experiments in Macroeconomics

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of naive expectations (following the classic analysis of Ezekiel (1938)). The authors consider three values for λ, for which the equilibrium is stable, unstable, or strongly unstable under naive expectations.15 Their assessment of the validity of the rationalexpectations assumption is based on whether market prices are biased (looking at the mean), whether price fluctuations exhibit excess volatility (looking at the variance), and whether realized prices are predictable (looking at the autocorrelations). Figure 1.2 shows a representative sample of prices and the autocorrelation of these prices from the three representative groups operating in the three different treatment conditions. This figure reveals the main finding of the study, which is that in all three treatments, the mean price forecast is not significantly different from the rational expectations value, though the variance is significantly greater (there is excess volatility) from the rational expectations value, σ2 = 0.25, in the unstable and strongly unstable cases. Even more interesting is the finding that the autocorrelations are not significantly different from zero (5% bounds are shown in the figures) and there is no predictable structure to these autocorrelations. The latter finding suggests that subjects are not behaving in an irrational manner in the sense that there is no unexploited opportunities for improving price predictions. This finding is somewhat remarkable given the limited information subjects had regarding the model generating the data, though coordination on the rational expectations equilibrium was likely helped by having a unique equilibrium and a limited price range (0, 10). Adam (2007) uses the learning to forecast methodology in the context of the twoequation, multivariate New Keynesian “sticky price” model that is a current workhorse of monetary policy analysis (e.g., Woodford 2003).16 In a linearized version of that model, inflation, πt , and output, yt , are determined by the system of expectational difference equations, e πt πt = a0 + a1 yt−1 + B + cvt e yt πt+1

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yt = y + vt π πt = yt−1 y where y and π represent steady-state values. Inflation lags output by one period due to predetermined (sticky) prices, and output deviates from its steady state only due to real monetary shocks. Thus a rational forecast model for πt should condition on yt−1 , that is, πt = α y + β y yt−1 . Of course, since subjects are given time-series data on both y and π , Adam imagines that subjects might alternatively use a simple (but misspecified) autoregressive forecast model of the form πt = απ + βπ πt−1 . Thus, the issue being tested here is not simply one of whether agents can learn to form rational expectations of future inflation but more importantly whether subjects, like econometricians, can find the correct specification of the reduced-form model they should use to form those rational expectations. Perhaps not surprisingly, the evidence on the latter question is somewhat mixed. Adam finds that in most of the experimental sessions, subjects forecast using the autoregressive inflation model and do not condition their forecasts on lagged output. However, he also shows that such behavior can result in a stationary, “restricted-perceptions” equilibrium that is optimal in the sense that autoregressive inflation forecasts outperform those that condition on lagged output. Adams further notes that this miss-specification in agents’ forecasts provides a further source of inflation and output persistence in addition to that implied by the model’s assumption of sticky price adjustment, a finding that has been elaborated upon by Davis and Korenock (2011). Bao and others (2013) study learning behavior in a cobweb model with a setup similar to that of Hommes and others (2007). However, they compare the performance of the learning-to-forecast experimental design with the alternative “learning-to-optimize” design, where subjects in the role of suppliers must directly choose the quantity, qti , of the good they wish to bring to the market in period t. In the latter case, the quantity of the six agents is simply summed up to give aggregate supply. Market clearing using the exogenous market demand yields the market price, pt . Subjects in this learning–to– optimize design are paid on the basis of their profit, pt qti − c(qti ), where c(·) is a known convex cost function. Bao and others have two further treatments: one in which subjects are asked to both form price forecasts and choose supply decisions and a second in which two subject teams are formed, with one team member performing the forecasting task that the other team member could use to determine the quantity task. In the latter two treatments, subjects are paid an equal weighted average of the payoffs from the forecasting and profit-maximizing tasks. Bao and others report that convergence to

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the rational-expectations equilibrium (REE) is fastest in the learning-to-forecast design and slowest and highly variable in the treatment where individual subjects must both forecast and choose quantity decisions. Dividing up the two tasks among team members greatly improves performance. These findings indicate that learning-to-forecast designs should be regarded as an upper bound on the speed and efficiency with which agents may learn a REE and that it may be more useful to think of the representative household or firm as a team of specialized actors. A second approach to boundedly rational expectation formation in macroeconomics takes into account the strategic uncertainties that can arise from interactions among heterogeneous agents. This approach is sometimes referred to as step-level reasoning and was motivated by Keynes’s (1936) famous comparison of financial market investors’ expectations to newspaper beauty contests of that era, in which participants had to select the 6 prettiest faces from 100 photographs. The winner of the contest was the person whose choices were closest to the average choices of all competitors. Keynes (1936, 156) noted that “each competitor has to pick, not those faces which he himself finds prettiest but those he thinks likeliest to catch the fancy of other competitors, all of whom are looking at the problem from the same point of view.” Keynes went on to observe that individuals might form expectations not just of average opinion, but might also consider what average opinion expects average opinion will be, and he further speculated that there might be some who practiced still “higher degrees” of reasoning. These observations concerning expectation formation were tested experimentally by Nagel (1995) in a game developed by Moulin (1986) that has since come to be termed the “beauty contest” game in honor of Keynes’s analogy. In Nagel’s design, a group of N = 15 − 18 subjects are each asked to “guess”— simultaneously and without communication—a real number in the closed interval [0, 100]. They are further instructed that the person(s) whose guess is closest in absolute value to a known parameter p times the mean of all submitted numbers is the winner of a large cash prize, while all other participants receive nothing. Nagel’s baseline experiment involves setting p < 1, for example, p = 23 . That game is straightforward to analyze: each player i wants to guess a number xi = p x¯ , where x¯ is the mean of all submitted numbers. Given this objective, in any rational expectations equilibrium we must have that xi = x¯ for all i . If p < 1, the only rational expectations solution is xi = x¯ = 0, that is, all N players guess zer o.17 To map this game into Keynes’s (1936) example requires setting p = 1, in which case any number in [0, 100] is a rational expectations equilibrium; the choice of p < 1 yields not only a unique equilibrium prediction but interesting insights regarding the extent of individual’s higher degrees of reasoning.18 Nagel’s experimental findings from three sessions of the p = 12 -mean game are shown in Figure 1.3, which reports the relative frequencies of number choices in the interval [0, 100].19 Notice first that the equilibrium prediction of 0 is never chosen. Second, there are large spikes in neighborhoods of the numbers 50, 25, and 12.5. A choice of 50 implies an expected mean of 100 in the p = 12 game and is thus barely rational—these players exhibit the lowest level of reasoning, which is often termed step, or level, 0. The somewhat more sophisticated level 1 types expect a mean of 50 and guess numbers that are 12 of their expectation around 25, while level 2 types are a step further ahead, anticipating a mean of 25 and thus guessing numbers around 12 or 13. A robust finding is that depths of reasoning in excess of level 2 are rarely observed; the winner of the beauty contest is typically a level-2 type. With repetition, subjects in these beauty contest games do eventually converge upon the unique rational expectations equilibrium prediction (0 in this case), but each

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individual’s process of expectation revision over time typically follows the same level of reasoning they exhibited in the first round played, for example, level k = 1 or 2 adjustment in each repetition. This experiment, which has now been replicated many times (see, e.g., Duffy and Nagel 1997; Ho, Camerer, and Weigelt 1998), reveals that in multiagent economies where all agents know the model, the common-knowledge-ofrationality assumption implicit in the rational expectations hypothesis may not hold. It further suggests that decision costs or cognitive constraints may lead individuals to adopt heuristic rules of thumb that result in predictable step-levels of belief revision, that is, systematic forecast errors. That convergence to equilibrium does obtain in the limit is reassuring but suggests that rational expectations might be best viewed as a long-run phenomenon. Summing up, we have seen some ways in which three microlevel assumptions that are mainstays of macroeconomic modeling—intertemporal optimization, time-consistent preferences/exponential discounting, and the rationality of expectations—have been tested in the laboratory, primarily in individual decision-making experiments. The evidence to date suggests that human subject behavior is often at odds with the standard micro-assumptions of macroeconomic models. The behavior of subjects appears to be closest to microassumptions, for example, intertemporal optimization, when subjects learn from one another or gather information on prices through participation in markets. The rational expectations model appears to be most reasonable in simple, univariate models (e.g., the cobweb model) as opposed to the more commonly used multivariate models. Hopefully, these and other experimental findings will lead to a reconsideration of the manner in which macroeconomic modelers characterize the behavior of their “representative” agents, though so far, there is not much evidence that such a change is imminent.

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3 COORDINATION PROBLEMS In the previous section, we focused on individual behavior in dynamic intertemporal optimization problems where the optimal rational expectations solution was unique. In many macroeconomic environments, this is not the case. Instead, multiple rational expectations equilibria exist, and the question is which of these equilibria economic agents will choose to coordinate upon. Laboratory experiments can be quite useful in this regard. Indeed, Lucas (1986) argued that laboratory experiments were a reasonable means of resolving such coordination problems because “economic theory does not resolve the situation [so] it is hard to see what can advance the discussion short of assembling a collection of people, putting them in the situation of interest, and seeing what they do.” Some coordination problems of interest to macroeconomists were previously addressed in Ochs (1995). In particular, that chapter surveyed experimental studies of overlapping-generations models, where money may or may not serve as a store of value (Lim, Prescott, and Sunder 1994) or subjects can select between low- or high-inflation equilibria (Marimon and Sunder 1993, 1994, 1995). Also included were experimental studies of stag-hunt and battle-of-the sexes games (surveyed also in Cooper (1999) and Bryant (1983)–type Keynesian coordination games (e.g., the minimum- and medianeffort games of Van Huyck , Battalio, and Beil (1990, 1991) and Van Huyck, Cook, and Battalio (1994).20 The coordination games literature delivered a number of important findings on when coordination success was likely to be achieved and when coordination failure was likely. Importantly, the results have been replicated by many other experimenters, leading to confidence in those findings. Rather than review those replications and extensions, in this section I report on more recent macrocoordination experiments. The environments tested in these experiments have a more direct resemblance to macroeconomic models than do the coordination games surveyed by Ochs (with the exception of Marimon and Sunder’s work on overlapping generations models). I also address some equilibrium-selection mechanisms or refinements that have been proposed for resolving macrocoordination problems and the experimental studies of those mechanisms and refinements. 3.1 Poverty Traps Lei and Noussair (2007) build on their (2002) experimental design for studying behavior in the one-sector optimal growth model by adding a nonconvexity to the production technology, resulting in multiple, Pareto-rankable equilibria. Specifically, the production function used to determine output in Noussair and Matheny (2000) and Lei and Noussair (2002) is changed to  f (kt ) =

Aktα

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if kt ≥ k ∗

where A < A and k ∗ is a threshold level of the aggregate capital stock that is known to all five subjects. The threshold switch in productivity is a simple way of modeling positive externalities that may arise once an economy reaches a certain stock of capital (physical or human; see, e.g., Azariadis and Drazen 1990). An implication is that there are now two stationary levels for the capital stock (and output) kl < k ∗ < k h , with kl

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representing the poverty trap and k h representing the Pareto efficient equilibrium. The dynamics of the system (under perfect foresight) are such that for k ∈ (0, k ∗ ), kl is an attractor, whereas for k ≥ k ∗ , k h is the attractor. The main experimental question is on which of these two equilibria subjects will learn to coordinate. One treatment variable was the initial aggregate level of the capital stock, either below or above the threshold level k ∗ and divided up equally among the five subjects. The other treatment condition was whether decisions were made in a decentralized fashion, with a market for the capital stock (subjects had different production technologies that aggregated up to the aggregate technology), or whether groups of subjects together made a collective consumption-savings decision, that is, playing the role of a social planner. In both cases, the indefinite horizon of the model was implemented using a constant probability of continuation, and subjects were paid on the basis of the utility value of the consumption they were able to achieve in each period. The main experimental finding is that in the decentralized treatment, the poverty-trap equilibrium is a powerful attractor; it is selected in all sessions where the initial aggregate capital stock is below k ∗ as well as in some sessions where the initial aggregate capital stock lies above k ∗ . There are some instances of convergence to the Pareto efficient stationary equilibrium k h but only in the decentralized setting, where the initial capital stock lies above k ∗ . In the social planner treatment, where five-subject groups jointly decide on consumption-savings decisions, neither of the two stationary equilibria were ever achieved; instead there was either convergence to a capital stock close to the threshold level k ∗ or to the golden-rule level that maximally equates consumption in every period. While the latter is close to the Pareto optimum, it is inefficient as it ignores the possibility that the economy may terminate (the rate of time preference is positive). Lei and Noussair (2007) conclude that additional institutional features may be necessary to both avoid and escape from the poverty-trap outcome. The possibility that various institutional mechanisms might enable economies to escape poverty traps is taken up in a follow-up experimental study by Capra and others (2009). These authors begin by noting that laboratory studies of the role of institutions in economic growth may avoid endogeneity problems encountered in field data studies (where it is unclear whether institutions cause growth, or vice versa) and more clearly explore environments with multiple institutions. The two institutions explored in this study are termed freedom of expression, which involves free discussion among subjects prior to each round of decision making and democratic voting, in which subjects vote on two proposals for how to divide output up between consumption and savings (future capital) at the end of each period. The baseline experimental design is essentially the same as the low initial capital stock treatment of Lei and Noussair (2007); there are five subjects who begin each indefinite sequence of rounds with capital stocks that sum up to an aggregate level that lies below the threshold level k ∗ .21 This initial condition for the aggregate capital stock is the same in all treatments of this study because the focus here is on whether subjects can escape from the poverty-trap equilibrium. At the start of a period, output is produced based on last period’s capital stock, and then a market for capital (the output good) opens. After the market for capital has closed, subjects independently and without communication decide on how to allocate their output between current consumption and savings (next period’s capital stock). In the communication treatment, subjects are free to communicate with one another prior to the opening of the market for capital. In the voting treatment, after the capital market has closed, two subjects are randomly selected to propose consumption/savings plans for all five agents in the economy; these

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proposals specify how much each subject is to consume and how much to invest in next period’s capital stock (if there is a next period). Then all five subjects vote on the proposal they prefer, and the proposal winning a majority of votes is implemented. In a hybrid treatment, both communication and voting stages are included together. The main findings examine the long-run values of two statistics for each session: (1) aggregate welfare from consumption (as measured by the sum of the period utility by all five agents i u(c ti )) and (2) the aggregate capital stock ( i kti ). Capra and others (2009) use an equation similar to (1) to estimate the asymptotic values of these two measures for each five-person economy.22 These estimated values are shown as squares in Figure 1.4, and the line segment through each square represents the 95% confidence region. The lower-left intersection of the dashed lines shows the poverty-trap level of aggregate welfare and capital, while the upper-right intersection of the two dashed lines shows the Pareto efficient level of aggregate welfare and capital. This figure reveals the main findings in the baseline treatment: consistent with Lei and Noussair, subjects are unable to escape from the poverty-trap outcome. The addition of communication or voting helped some, though not all, economies to escape from the poverty trap. In the hybrid model, which allows both communication and voting, the experimental economies appear to always escape from the poverty trap (95% confidence bounds exclude poverty-trap levels), and these economies are closest to the Pareto efficient equilibrium levels for welfare and the capital stock. Capra and others argue that binding consumption/savings plans as in the voting treatment are important for achieving aggregate capital stock levels in excess of the threshold level, while communication makes it more likely that such consumption/savings plans are considered in the first

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place; not surprisingly then, the two institutions complement one another well and lead to the best outcomes. While this experimental design involves a highly stylized view of the institutions labeled “freedom of expression” and “democratic voting,” the same critique can be made of the neoclassical model of economic growth. The experimental findings suggest that there may be some causality from the existence of these institutions to the achievement of higher levels of capital and welfare, though the opposite direction of causality from growth to institutions remains an important possibility. More recently, macroeconomists have emphasized the role of human capital accumulation, so it would be of interest to consider whether subjects learn to exploit a positive externality from a highly educated workforce. And while several other studies have pointed to the usefulness of communication in overcoming coordination problems (e.g., Blume and Ortmann 2007; Cooper et al. 1992), these have been in the context of strategic form games. While the results of those studies are often cleaner, in the sense that the game is simple and communication is highly scripted, the study by Capra and others implements institutional features in a model that macroeconomists care about, and this may serve to improve the nascent dialogue between experimentalists and macroeconomists. 3.2 Bank Runs Another important coordination problem that has been studied experimentally in the context of a model that macroeconomists care about is Diamond and Dybvig’s (1983) coordination game model of bank runs. In this three-period intertemporal model, depositors find it optimal to deposit their unit endowment in a bank in period 0, given the bank’s exclusive access to a long-term investment opportunity and the deposit contract the bank offers. This deposit contract provides depositors with insurance against uncertain liquidity shocks; in period 1, some fraction of depositors learn they have immediate liquidity needs (are impatient) and must withdraw their deposit early, while the remaining fraction learn they are patient and can wait to withdraw their deposit in the final period 2. The bank uses its knowledge of these fractions in optimally deriving the deposit contract, which stipulates that depositors may withdraw the whole of their unit endowment at date 1, while those who wait to withdraw until period 2 can earn R > 1. While there exists a separating, Pareto efficient equilibrium where impatient types withdraw early and patient types wait until the final period, there also exists an inefficient pooling equilibrium, where uncertainty about the behavior of other patient types causes all patient types to mimic the impatient types and withdraw their deposits in period 1 rather than waiting until period 2. In the latter case, the bank has to liquidate its long-term investment in period 1; depending on the liquidation value of this investment, it may have insufficient funds to honor its deposit contract in period 1. The possibility of this bank-run equilibrium is the focus of experimental studies by Garratt and Keister (2009), Schotter and Yorulmazer (2009), Madiés (2006), and Arifovic, Jiang, and Xu (2013). All of these experiments dispense with inducing the two player types and focus on the decisions of the single “patient” player type alone, who is free to choose whether to run on the bank (mimicking an impatient type) or not, that is, they all focus on the pure coordination game aspect of the problem. Garratt and Keister (2009) study the coordination game played by five subjects who have $1 deposited in a bank and must decide at one or more opportunities whether to withdraw their $1 or leave it deposited in the bank, potentially earning a higher return of $1.50. Following each withdrawal opportunity, subjects learn the number of players

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TABLE 1.2: Bank-run coordination game payoffs. Source: Garratt and Keister (2009). Hypothetical No. of Withdrawl Requests

Amount Each Requester Would Receive

Projected Payment to Each Depositor

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n/a $1 $1 $1 $0.75 $0.60

$1.50 $1.50 $1.50 $0 $0 n/a

in their group of five (if any) who have chosen to withdraw. As treatment variables, Garratt and Keister varied the number of withdrawal opportunities (one or three) and the number of early withdrawals a bank could sustain while continuing to offer those who avoided withdrawal a payoff of $1.50 (i.e., variation in the liquidation value of the bank’s long-term investment). Table 1.2 provides one parameterizations of Garratt and Keister’s bank-run game. Garratt and Keister report that for this baseline game, regardless of the liquidation value of the long-term investment, no group ever coordinated on the “panic equilibrium” (five withdrawals) and a majority of groups coordinated on the payoff dominant equilibrium (zero withdrawals). In a second treatment that more closely implements the liquidity shock in the Diamond-Dybvig model, Garratt and Keister added “forced withdrawals” to the baseline game: at each withdrawal opportunity, there was a small known probability that one randomly selected player would be forced to withdraw. However, whether a withdrawal was forced or not was unknown to subjects. The probabilities of forced withdrawals were chosen such that there continued to exist a payoff dominant equilibrium in which no player ever voluntarily withdrew at any withdrawal opportunity (if all adhered to this strategy, they would earn an expected payoff greater than $1) as well as a panic equilibrium where all withdraw. Garratt and Keister report that with forced withdrawals (liquidity shocks), the frequency of voluntary withdrawals and coordination on the panic equilibrium is significantly greater relative to the baseline treatment with unforced withdrawals. This increase in panic behavior was particularly pronounced in the forced-withdrawal treatment where subjects had multiple withdrawal opportunities and could condition their decisions on the prior decisions of others. An implication of this finding is that panic behavior may require some conditioning on the decisions of others, suggesting that the bankrun phenomenon is perhaps best modeled as a dynamic game, as opposed to the simultaneous-move formulation of Diamond and Dybvig (1983). Schotter and Yorulmazer (2009) arrive at a similar conclusion, using a somewhat different experimental design. Theirs involves a group of six subjects deciding in which of four periods to withdraw their deposit of $K in the face of uncertainty concerning both the withdrawal decisions of the other five subjects as well as the type of bank in which all six have invested their deposits. Subjects know that there are five possible bank types, that each type is equally likely to be drawn for the duration of each four-period game, and that the mean return across types is r ∗ .23 While the bank type is unobservable, the “promised” return is fixed at 12% per period, while the mean return r ∗ was varied

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across sessions, either 0.07, 0.08 or 0.14. Subjects were told that if they kept their $K deposit invested for  periods, they could earn a return of $(1.12) K if the bank has sufficient funds left in period , but if not, the bank would pay all those withdrawing in that period an equal share of remaining funds on hand (if any). Subjects had to choose in which of the four periods to withdraw their money, with withdrawal being irreversible. The authors think of this as a model of a bank run in progress (the precipitating event is left unmodeled) and are interested in exploring three factors that may slow or hasten the period in which deposits are withdrawn. A first factor is whether the withdrawal decision across the four periods is implemented as a simultaneous-move normal-form game or as an extensive-form game; in the former case subjects specify the period in which they want to withdraw their funds (1, 2, 3, or 4), while in the latter case subjects make withdrawal decisions period by period and may condition on the prior period withdrawal decisions (and in one treatment, the amounts earned) by others. The second and third factors are the use of deposit insurance to delay or slow down the run or the presence of insiders who know the mean return r ∗ of the banks and may, through their actions, persuade other uniformed subjects to run early or wait. Schotter and Yorulmazer (2009) find that bank runs are less likely to be severe (withdrawal occurs later, e.g. in period 3 or 4) when r ∗ is known to be greater than the bank’s promised return of 12%. For fixed r ∗ , runs are also less severe in the extensiveform version of their model, when agents can condition on the decisions of others and there is a high degree of information, in that subjects also know the amounts that others have received.24 This finding is interesting in that theory does not predict that the game form should matter; the fact that it does again points to the value of thinking of bank runs as dynamic rather than static games. They further show that partialdeposit insurance may work to diminish the severity of bank runs, as can the presence of some depositor insiders who know the type of bank with which funds have been invested. Madiés (2006) examines bank runs as two-period pure coordination games repeatedly played (thirty repetitions) by larger groups of ten subjects. Madiés varied (1) the difference in payoffs from early versus late withdrawals, (2) the number of early withdrawals a bank could sustain while continuing to offer those who avoided an early withdrawal their promised late-withdrawal payment, and (3) the role played by suspension of deposit availability (implemented as suspension of activity during the experiment to calm the panic) or deposit insurance of either 25% or 75% coverage in arresting bank runs. Among other findings he reports that pure panic equilibria, where all ten subjects run in the first period, are rare under all treatment conditions and that partial runs are much more common, even though such partial runs are not equilibria of the model. Further, threatened suspensions of deposit availability are rather effective at preventing bank runs, while partial-deposit insurance is essentially ineffective. Arifovic, Jiang, and Xu (2013) also study two-period bank runs as pure coordination games with groups of ten subjects. They fix the pure strategy run equilibrium payoff to 1 and the pure strategy no-run equilibrium payoff to 2 and systematically vary the shortrun return to early withdrawal, which can be reinterpreted as a coordination parameter, η, specifying the minimum fraction of depositors who must withdraw late to equalize the payoffs earned from early and late withdrawals. Their main finding is that runs reliably occur when η is 0.7 or greater, that is, when at least 70% of subjects must withdraw late in order to achieve a payoff that is at least as high as the payoff from withdrawing early. One novelty of their design is that they do not use neutral language and frame the game played as a decision of when to withdraw deposits from a bank.

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The issue of the contagious spread of a bank run from one location to another is addressed experimentally by Corbae and Duffy (2008). They study a two-stage, fourplayer game. In the first stage, players simultaneously propose to form links with one another; mutually agreeable links are then implemented and comprise the set of each player’s “neighbors.” Corbae and Duffy interpret the players as “banks” connected to one another via interbank reserve deposits that can serve to insure against risk. (à la Allen and Gale 2000). In the second stage, each player plays τ rounds of an n-person, equal-weighted-payoff “stag”-hunt game with his n = 1, 2, or 3 neighbors. As in Garratt and Keister (2009), one of the four-players is “shocked”—that is, randomly must play the inefficient “hare” or run strategy in all rounds of the second-stage game. Corbae and Duffy define a contagion as a movement by all players away from the Pareto efficient stag equilibrium to the inefficient hare equilibrium. While it is possible for subjects to implement a complete network of links (the four players have three links each) that provides insurance against the risk of being linked to a player forced to panic, as when all unshocked players play stag, Corbae and Duffy show that such a network configuration is not an equilibrium due to the free-rider problem. Instead, the network configurations that are predicted to emerge are bilateral networks (twoplayer networks, where each player has a single link), which serves to limit the spread of the bank-run outcome. Corbae and Duffy report experimental evidence that is broadly consistent with this prediction. Starting groups of four subjects out in different exogenous network configurations and then in subsequent games allowing them to choose the players they want to link to, they report that subjects consistently move in the direction of choosing to have a single link to one other player. Under this bilateral network, the bank-run equilibrium is isolated to just one of the two-player networks; the other network achieves the efficient, payoff-dominant equilibrium. Summing up, we have discussed two kinds of macroeconomic-coordination experiments, poverty traps and bank runs. In the poverty-trap model, the question of interest is how to get subjects to move from an inefficient equilibrium to an efficient one. We might think of this as a good contagion. In the bank-run model, the question of interest is precisely the opposite: how to keep funds deposited in a bank longer (earning higher returns) and avoid a bad contagion to an inefficient panic equilibrium. Both types of movements are difficult to achieve in the laboratory. In the case of movement from an efficient to an inefficient equilibrium, it seems necessary to force some players’ hands in order to precipitate a transition to the inefficient outcome; that finding suggests that the precise mechanism precipitating a bad contagion has yet to be discovered. We next explore experimental tests of two mechanisms that macroeconomists have used to resolve coordination problems. 3.3 Resolving Coordination Problems: Sunspots In the bank-run coordination game, the question of equilibrium selection is left unmodeled. Diamond and Dybvig (1983) suggest that depositors might use realizations of some commonly observed, nonfundamental random variable, or “sunspot” in the language of Cass and Shell (1983) and Azariadis (1981), to resolve the question of the equilibrium on which coordinate.25 The notion that agents might coordinate on such variables is not so far-fetched. Roos (2008), for instance, provides survey evidence showing that students overweight realizations of nonfundamental factors relative to more fundamental factors in assessing the impacts of those factors on short-run macroeconomic performance in Germany. However, without the controlled conditions

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of the laboratory, it can be difficult to say what factors are truly fundamental, which are less so, and which are purely extrinsic and nonfundamental. Three experimental studies of sunspot variables as coordination devices have been conducted: Marimon and others (1993), Duffy and Fisher (2005), and Fehr, Heinemann, Llorente-Saguer (2013); we describe each in turn. Marimon and Sunder (1993) implemented a two-period overlapping generations environment where, if agents have perfect foresight, there are multiple equilibria: an interior steady state and a two-period cyclic equilibrium. Subjects in the role of young agents formed price expectations that determined current prices, given the nonlinear e ). Thus given price expectations, subjects’ optimal consumption model, pt = φ( pt+1 and savings in the form of real money balances were determined (as in Marimon and Sunder 1993, 1994). Marimon and Sunder hoped that subjects would use realizations of a sunspot variable to coordinate their expectations on the cyclic equilibrium. Their sunspot variable consisted of a blinking cube on subjects’ computer screens. The color of this cube alternated every period between red and yellow. Marimon and Sunder found that subjects essentially ignored the sunspot variable realizations and simply coordinated on the steady states. They later tried to add a correlation between the sunspot variable and a real endowment shock (alternating the size of the young generation between three and four subjects, i.e., three-four-three-four), but this also did not lead to coordination on the sunspot variable when the endowment shock was shut off. Duffy and Fisher (2005) consider a simpler, partial equilibrium framework that abstracts from a number of conceptual difficulties (e.g., implementing an infinite horizon). In this simple and static environment, there are two equilibria that differ only in terms of the equilibrium price level; the equilibrium quantity is the same in both. The experimental design involves five buyers and five sellers, each with two units to buy or sell. Buyers seek to maximize consumer surplus (valuation − price), while sellers seek to maximize producer’s surplus (price − cost). Further, each buyer (seller) had two possible valuations (costs) for each of his or her two units. If the state was high, each buyer’s (seller’s) profits were calculated using his or her two high valuations (costs). If the state was low, each buyer’s (seller’s) profits were calculated using his or her two low valuations (costs). The two sets of valuations/costs used in the experiment are shown in Figure 1.5. Buyers are B1–B5 and sellers are S1–S5. Market clearing prices with high demand and supply are in the interval [190, 210]. Market clearing prices with low demand and supply are in the interval [90, 110]. The equilibrium quantity is always six units bought and sold. Two market-clearing mechanisms were considered—the standard double auction, where bids and asks can be observed in real time, and a sealed-bid variant known as a call market, where bids and asks are submitted simultaneously, bids are sorted from highest to lowest and asks, from lowest to highest, and a single market clearing price is determined by the intersection of demand and supply (if there is one). All buyers with bids above the market price get to buy their units, provided there are enough units for sale. All sellers with asks below the market price get to sell their units provided their is enough demand. The state of the world was determined by the median traded price in the double auction or by the market-clearing price in the call market. If either price was greater than or equal to 150, then the high state was declared, and subjects use high valuations or costs in determining their surplus (payoff). Otherwise the low state was declared, and low valuations and costs were used in the determination of payoffs. Thus the situation is akin to one in which there are multiple equilibria, each supported by different beliefs about the likely state of the world.

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270 260

B5

250

B4

240 230

S4

B2

220

B1

210

S3

B1 S2

200

B2

190

Price in Francs

High supply

S5

B3

S1

180

S1

B3

S2

170 160 150 140

S5

S4

B1

B2

130

B4

S3

B5

B3

S1

Low supply

S2

B4

120

High demand

B5

110

S3

B5 S4

100

B4

90

S1

80

S1

B3

S2

70

B2

S3

60

B1

Low demand

S4

50

S5 0

1

2

3

4

5

6

7

8

9

10

Quantity

Figure 1.5: Induced high and low demand and supply in Duffy and Fisher (2005).

Duffy and Fisher’s sunspot variable was one of two possible announcements made prior to each of ten four-minute trading periods. The announcement chosen was determined by publicly flipping a coin. In one treatment, if the coin flip was heads, the public announcement was, “the forecast is high”, while if the coin flip was tails, the public announcement was, “the forecast is low”, and this scheme was public knowledge. Duffy and Fisher report that in sessions using a call-market-clearing mechanism, subjects perfectly coordinated on the high-price equilibrium when the forecast was high and on the low-price equilibrium when the forecast was low—that is, the sunspot variable was shown to matter for economic volatility. On the other hand, under the double-auction-market-clearing mechanism, the sunspot announcements only sometimes served to coordinate subjects on the high or low equilibrium. Duffy and Fisher argue that the reason for this difference lies in the real-time information that was available in the double auction; subjects could see bids and asks as they occurred and could use this information to attempt to engineer an equilibrium outcome for prices (high or low) that was more favorable to them.26 Thus the coordinating mechanism provided by the sunspot could be undone by the real-time information on bids, asks, and trade prices. The same was not possible in the call market, where bids and asks

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had to be submitted simultaneously; hence the sunspot variable played an important coordinating role in the environment. Duffy and Fisher further show that the semantics of the sunspot variable matter: replacing “the forecast is high” or “low” with “the forecast is sunshine” or “rain” eliminated the sunspot variable as a coordinating mechanism in the call market. Fehr, Heinemaan, and Llorente-Saguer (2013) study the emergence of sunspot equilibria in an even simpler setting, a two-player coordination game, where the two players i ( j ) must simultaneously choose numbers ai (a j ), from the interval [0, 100], and each earns a payoff that is a quadratic function of the squared deviation, (ai − a j )2 . The focus of this study is on the nature and number of the extrinsic signals, whether they must be public or could be privately observed and whether there is one signal or two. In most treatments a common extrinsic signal, Z, is known to be a random drawn from the binary distribution {0, 100} at the start of each of 80 periods. In some treatments, the value of Z is publicly observable to both players, while in other treatments subjects receive a private noisy signal of the value of Z with a given precision, or a public and private signal, or two public signals, all from the same binary distribution. In a control treatment, subjects receive no signal and quickly coordinate on the risk-dominant choice of 50 (the midpoint of the action space). When there is a single public signal, subjects play according to a sunspot equilibrium, choosing numbers corresponding to the realized public signal 0 or 100. They have no difficulty continuing to play according to a sunspot equilibrium with two public signals; when the signals differ, they choose the average of the two signals, 50, and thus coordinate on play of a “three-cycle.” The sunspot equilibrium breaks down when subjects receive a public and a private signal, as subjects are unable to ignore their private signal and, consequently, their play converges to the risk dominant strategy of always choosing 50. Most interestingly, they report that if subjects receive only private signals of Z (no public signal) and these private signals are sufficiently precise as to the true value of Z so that the private signals are highly correlated with one another, then subjects continued to choose numbers according to the private signal they received even though such actions are not consistent with any pure sunspot equilibrium. This is an interesting empirical finding, suggesting an avenue by which the notion of a sunspot equilibrium might be more general than theory currently admits. Further research on this topic might seek to understand how the mapping from sunspot variable realizations to the action space matters in getting subjects to coordinate on sunspot equilibria; for instance, does the dimensionality of the signal space need to be small relative to the action space, and if so, how small? It would also be of interest to consider sunspot equilibria that are not simply randomizations over two certainty equilibria. 3.4 Resolving Coordination Problems: The Global Game Approach Another view of multiple equilibria in macroeconomic modeling is that the equilibrium beliefs in support of these equilibria may not be as indeterminate as theory supposes. As Morris and Shin (2001) argue, these indeterminacies arise from assuming that economic fundamentals are common knowledge and that individuals are certain of the behavior of others in equilibrium. Relaxing these assumptions—for example, by introducing some uncertainty about fundamentals—can remove the multiplicity, à la the Carlsson and van Damme’s (1993) global game approach for 2 × 2 games.27 The resulting game is one in which individuals adopt a unique threshold strategy—when fundamentals are

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weak, individuals are pessimistic about others’ beliefs and the resulting outcome is poor, as in the bank run equilibrium. However if fundamentals are strong, so will be beliefs about others’ beliefs, and the resulting outcome will be good, as in a payoff-dominant equilibrium. This correlation between fundamentals and outcomes is missing from the sunspot approach.28 Heinemann, Nagel, and Ockenfels (2004) conducted the first experimental test of the global game approach to resolving equilibrium multiplicity in the context of a speculative currency attack model developed by Obstfeld (1996) and Morris and Shin (1998). Prior to the start of each (2 × n)-player game, a payoff relevant random variable Y is drawn from a uniform distribution with known support. This variable represents the fundamentals of the economy with higher (lower) values of Y representing worse (better) fundamentals. In the complete-information (CI) treatment, this variable is known to all fifteen subjects, while in the private-information (PI) treatment, the value of Y is not known, but each of the fifteen subjects receives noisy signals of Y, X i that are uniform random draws from the known interval [Y − , Y + ], where  is small. Subjects must then decide between two actions, A and B, where A is a safe choice resulting in a fixed payoff F (equivalent to not running or not attacking a currency). The other choice, B, is a risky choice (equivalent to attacking a currency, joining a rebellion, etc.), the payoff from which depends on the total number of players who choose B as determined by a monotonically decreasing function f (Y). If less than f (Y) agents choose B, all those choosing B, earn 0 (the attack fails), while if at least f (Y) agents choose B, then all those choosing B earn Y points (the attack succeeds). Consistent with the theory, the distribution of Y-values is chosen so that there exist values of Y ≤ F for which it is a dominant strategy to choose A; similarly, there exist values of Y ≥ f −1 (1) for which a single individual can guarantee the success of an attack by choosing B, so that it is dominant for all to do so. For Y values in (F , f −1 (1)), under complete information, there are multiple equilibria: all choose A or all choose B, both of which can be supported by the belief that all others will choose A or B. However, in the incomplete-information game, there exists a unique, threshold value of the noisy signal X for which all subjects should attack (choose B) if their signal is above the threshold and not attack otherwise. Taking the limit as  → 0, it is possible to find a similar threshold Y ∗ in the complete-information game. The main question pursued by Heinemann, Nagel, and Ockenfels (2004) is whether the complete-information game, with its multiplicity of equilibria, is more unstable than the private-information game and whether subjects adopt threshold strategies consistent with the global-game threshold prediction. They report that subjects do appear to adopt threshold strategies in both the private- and complete-information cases, and these estimated thresholds generally lie below the global game predictions X ∗ or Y ∗ but are higher than the payoff-dominant prediction of choosing B whenever Y > F . The most interesting finding is in the complete-information treatment, where Y is publicly known and there are, in principle, multiple equilibria. In that treatment Heinemann and others report less variance in entry decisions than in the incompleteinformation treatment and greater coordination on a common threshold in the former as compared with the latter. Heinemann and others conclude that “with public information the central bank has more control over trader’s beliefs than when they get private information from other sources.” The global-game refinement has been experimentally examined in several other studies. Cornand (2006) adds two treatments, one with a private and a public signal and a second with two noisy public signals. She reports that subjects overreact to the

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public signal when they also receive a private one but that predictability of an attack is higher in that case as compared to the case of two noisy public signals. This finding suggests that if officials are going to make public announcements, they would do well to coordinate on a single message. Cabrales, Nagel, and Rodriguez-Mora (2007) test the global-game theory in two-person games with a more discrete state space. They find greater coordination on the global-game prediction in the incomplete-information case and on the payoff-dominant equilibrium in the complete-information case. Heinemann, Nagel, and Ockenfels (2009) augment their original (2004) design to additionally collect data on subjects’ degree of risk aversion and their subjective beliefs regarding the choices of other members of their group. They use data from this within-subject design to report several findings, including the observation that more risk-averse agents are less likely to play the risky choice B and that subjects under- (over-) estimate the probability of successful coordination when the hurdle function f (Y) requires a low (high) number of players to choose B. Additionally, they use their experimental data to estimate and compare two models of strategic uncertainty that make use of the global games refinement—one involving uncertainty about monetary payoffs and the other involving uncertainty about risk attitudes—and find that both models deliver good inand out-of-sample performance. Duffy and Ochs (2012) embed Heinemann, Nagel, and Ockenfels’ (2004) design in a dynamic setting where subjects have multiple periods in which to decide whether to attack or not and may condition their decision on the prior decisions of others. They report little difference in the thresholds used in the dynamic game as compared with those used in the static game, even if in the dynamic game there are costs associated with a delayed choice of B. Finally, Szkup and Trevino (2011) use Heinemann and others’ design to examine the implications for the global-game solution of adding costly information acquisition—specifically, a choice of the precision of the private signal received, with more precise signals being more costly. They report that only 30% of subjects choose the equilibrium middle level of precision, and counter to their theory, subjects who pay a higher cost for more-precise signals generally choose B more often, a result they attribute to dynamic game considerations. Summarizing, we have considered laboratory evidence on several mechanisms for selecting from among multiple equilibria in macroeconomic models, including communication, voting, sunspots, and threshold strategies based on the global game refinement. The laboratory is a natural testing ground for these mechanisms, as other confounding factors can be minimized and attention can be focused on the hypothesized coordination device. The experimental findings to date suggest mixed support for any single mechanism as the means by which individuals actually go about solving coordination problems. Still, many improvements on these studies remain to be conducted, and it is likely that with further study we will have a better sense of which mechanisms work best in particular settings.

4 FIELDS IN MACROECONOMICS In the following sections we review experimental studies that address issues in a particular field of macroeconomics. The three macroeconomic fields that have attracted to most laboratory study are monetary economics (which has attracted the greatest attention to date), labor economics and international trade and finance. In focusing on specific topics in macroeconomics, these laboratory studies follow the macroeconomic

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literature which often abstracts from certain sectors of the macroeconomy altogether, (e.g., the government sector) in order to better address a specific macroeconomic question (e.g., why money is used). A few studies have attempted to combine two or more sectors of the macroeconomy and these are reviewed in the last subsection on multi-sectoral macroeconomics. 4.1 Monetary Economics What is the role of money in the macroeconomy? Traditionally, money has been assigned three roles: as a store of value, as a medium of exchange, and as unit of account. As I have observed earlier (Duffy 1998), much of the theoretical and experimental literature on money can be divided up according to the primary role of money. Studies of money as a store of value focus on the question of how an asset with no intrinsic value (i.e., fiat objects) may be used as storage devices, even though they are subject to depreciation over time due to inflation. As a medium of exchange, money must serve as a store of value, but the opposite is not true; there are many stores of value that are not media of exchange. Thus researchers interested in money as a medium of exchange have sought to understand the frictions that give rise to use of certain stores of value as media of exchange. Finally, as the prices of goods and services are all stated in monetary terms, money’s role as a unit of account is important for efficient decision making. In addition to the primary roles of money, experimental studies can also be categorized according to the friction that enables money to be valued in equilibrium along with the mechanism by which exchange of money for goods takes place. Table 1.3 summarizes the approaches to studying money in the laboratory that are reviewed in this section. The store-of-value role of money is the focus of an early experimental study by McCabe (1989). That study focuses on whether fiat objects will be used as stores of value in an economy with a known finite end, at which time the fiat object ceases to have any continuation value. McCabe’s design involves three player types and six rounds of play. One of the three player types is initially endowed with a durable ticket (fiat money) that can be exchanged for one unit of any good and the other two types are endowed with nondurable goods. Exchanges of tickets for goods occurs via a centralized clearinghouse with known rationing rules; barter exchanges of goods for goods are not allowed, so effectively a cash-in-advance constraint operates. Holding a good at the end of a round yields different redemption values to different player types (either $0.50, $0.25, or $0.0) and the endowments of these goods also varies across player types. If this game continued without end, the use of tickets would enable the efficient exchange of goods to types who most value those goods (direct barter is ruled out). However, since the game is known to have a finite end at which point tickets have zero value, via a backward induction argument, tickets should never be accepted in trade. McCabe, however, reports that tickets are indeed accepted, though with some falloff near the end of each six-round game. Despite repeating the six-round game ten to twenty times with the same group of subjects, tickets continue to circulate in early rounds of the game. McCabe did eventually succeed in eliminating all trade in tickets but only after bringing back the same group of subjects for two further sessions, each a week apart. McCabe suggests that the inexperienced subjects’ use of tickets may be sustained by strong homegrown prior beliefs that money-type objects such as tickets will be accepted in exchange as they are in everyday life.

Primary Role of Money Store of value Store of value Store of value Store of value Store of value Medium of exchange Medium of exchange Medium of exchange Medium of exchange Medium of exchange Medium of exchange Medium of exchange Medium of exchange

Study

McCabe (1989) Deck et al. (2006) Hens et al. (2007) Marimon and Sunder (1993, 1994, 1995) Bernasconi and Kirchkamp (2000) Camera et al. (2006) Brown (1996) Duffy and Ochs (1999, 2002) Duffy (2001) Anbarci et al. (2013), Berentsen et al. (2013) Camera and Casari (2014) Duffy and Puzzello (2014a,2014b)

TABLE 1.3: Characteristics of experimental studies of money.

Cash in advance Cash in advance Cash in advance Overlapping generations Overlapping generations Overlapping generations Random matching Random matching Random matching Directed search Random matching Random matching Random matching

Friction Enabling Money

Clearinghouse with rationing Double auction Clearinghouse with rationing Centralized mkt. clearing Centralized mkt. clearing Double auction Bilateral exchange Bilateral exchange Bilateral exchange Posted prices Bilateral exchange Bilateral exchange Bilateral exchange

Exchange Mechanism

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Market A Good A

Good A $

Type B

Good A

$

$

Government $

$

Good B

Good B

Type A $ Good B

Market B Figure 1.6: Experimental design. Source: Deck, McCabe, and Porter (2006).

Deck, McCabe, and Porter (2006) follow up on the McCabe study by adding government agents who, unlike the other two player types in their study, are not budget constrained as to the quantity of tickets they can redeem for goods (i.e., they can “print money” ). The two other player types, A and B, are endowed each period with amounts of goods B and A, respectively, but profit from acquiring certain amounts of goods A and B, respectively; unlike the government-player types, the A- and Btype players are liquidity constrained and must resort to trading the good they are endowed with in the two double-auction goods market for tickets in order to buy the good they desire to consume. Figure 1.6 provides an illustration. As barter is disallowed, the friction giving rise to a demand for money is a cash-in-advance constraint. As in McCabe’s study, there is a finite horizon that is varied, and in some treatments where money is “backed,” tickets have a final cash redemption value. In treatments without government agents, subjects use money as a store of value (and, hence, as a medium of exchange) regardless of whether it is backed or not and despite the finite horizon, as in McCabe (1989). The addition of the government agents who are not budget constrained and who desire additional units of both goods leads to a rapid escalation of the price level, which Deck and others term a hyperinflation. This outcome arises in part because the government agents’ ability to print tickets leads to a rapid increase in the supply of money, but Deck and others emphasize that the erratic means by which the government introduces newly printed money also corrupts the information revealed in market-traded prices. The hyperinflation finding is consistent with the work of Sargent (1983), who attributes historical episodes of hyperinflations to excessive fiat money creation. Deck (2004) provides further experimental evidence that hyperinflations of the Deck, McCabe, and Porter (2006) variety can be ended by either making the currency convertible or by limiting government spending to current tax receipts (a balanced budget). Such mechanisms are also consistent with the historical record on ending hyperinflations. Similar to the Deck and others’ study, Hens, Schenck-Hoppe, and Vogt (2007) address whether a fiat object can achieve a stable value, facilitating its use as a medium of exchange. However, their focus is on whether an optimal quantity of fiat money can be achieved. They present a model inspired by the Capitol Hill Baby Sitting Coop, a natural experiment in the 1970s in which approximately 150 Capitol Hill couples exchanged babysitting duties with one another for coupons (Sweeny and Sweeny 1977). The co-op organizers found that too few coupons led to coupon hoarding (precautionary savings?), resulting in low demand for babysitting and a collapse of the

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system. An increase in coupons led to a thriving exchange of babysitting services, but eventually, overissue of coupons resulted in excess demand for babysitting and, given the fixed price of 1 coupon = 12 hour of babysitting, led again to a collapse of the system. Hens and others first develop a model wherein individuals face preference shocks for a perishable single good (they have either a high or low value for it), eliminating barter, and must choose whether to be buyers or sellers of the good in each period. Buy or sell decisions are made simultaneously via a centralized mechanism with a long side of the market rationing rule. To buy a good, an individual must have money on hand, so a cash-in-advance constraint gives money value. Sales of goods augment an individual’s money holdings; prices are fixed. The unique equilibrium prediction of their rational expectations, forward-looking, infinite-horizon model is that subjects who hold no money always offer to sell goods for money, regardless of their period valuation for the good. Whether subjects choose to buy goods using money depends on their period valuation for the good. In the high-valuation state, exchanging money for goods is a dominant strategy. However, in the low-valuation state, subjects should use money to buy goods only if their money holdings are sufficiently high; if below a critical level m, subjects should sell goods to acquire more money. This critical level of money holdings is related to the supply of money, which is exogenously chosen. Hens and others show that there is a unique optimal quantity of money that maximizes the number of trades possible (i.e., no trader is rationed), given that players are playing according to the optimal buy/sell strategy. Their nicely designed experiment tests these predictions in a two stages. In the first stage subjects participate in individual decisionmaking experiments, where they make buying and selling decisions and do or do not face exogenous rationing with regard to whether their buy or sell orders are satisfied; this gives subjects experience with the clearinghouse mechanism. In the second stage, subjects participate in a six-player market game, where the probabilities of successfully buying or selling (rationing) using the centralized mechanism depend on the decisions of all agents. Hens and others report that subjects’ strategies coincided well with the forward-looking optimal strategies of the theory. Furthermore, exogenous increases in the supply of money led first to an increase in the volume of trade, followed by a decrease in the volume of trade as the supply of money was further increased, with the peak corresponding to the predicted optimal quantity of money. The latter finding thus replicates the history of the Capitol Hill Baby Sitting Co-op and nicely illustrates the difficulty central banks face of determining an optimal quantity of money. Of course, the optimal quantity of money is complicated by the fact that the coupon price of babysitting is fixed, which is more typical of trade circles where fairness is a concern and less so of actual monetary systems. A second friction giving rise to the use of money as a store of value is that of overlapping generations (OG) of trading agents. As is well known (Shell 1971), the double infinity of dated goods and traders in the OG model violates the standard assumptions of general equilibrium analysis and can give rise to competitive equilibria that are not Pareto optimal, in violation of the second welfare theorem. This possibility provides a role for money (or other stores of value, e.g., social security promises) as Pareto improving devices (Samuelson 1958). Lim, Prescott, and Sunder (1994) were the first to implement an OG model of money in the laboratory with the aim of studying money as a store of value and the dynamics of price behavior. Further experimental studies involving monetary OG models that focused on questions of equilibrium selection were performed by Marimon and Sunder (1993, 1994) and are reviewed in the first volume of the Handbook of Experimental Economics by Ochs (1995). Here I want

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to review two OG money model experiments that have appeared more recently and which build on the design of Marimon and Sunder. Bernasconi and Kirchkamp (2000) reexamine Marimon and Sunder’s experimental design regarding how young agents determine the fraction of youthful endowment they should save in the form of money for later purchase of old-age consumption. Marimon and Sunder (1993) had subject cohorts alternate between youth and old age in their indefinitely repeated two-period OG model. Each subject i who was “young” in period t forecast the gross inflation rate (π ) of the price level between t and t + 1, E i,t−1 πt+1 = E i,t−1 (Pt+1 /Pt ), drawing on the past history of the aggregate price level, P , through period t − 1. Based on this forecast, the computer program determined each subject i ’s optimal savings, s i,t , given their lifetime utility function and budget constraint. As savings had to be held in the form of money, equilibrium market clearing required that the aggregate demand for real savings, i s i,t , equal the supply of real money balances Mt /Pt . Since the money supply Mt is exogenously determined, this market-clearing condition determines the period t price level, Pt . Bernasconi and Kirchkamp were critical of the optimal derivation of individual savings based on inflation forecasts. The “learning how to forecast” design of Marimon and others is only one dimension of forwardlooking rational expectations models, the other being the ability of agents to solve intertemporal optimization problems given their forecasts. Bernasconi and Kirchkamp thus modified the design of Marimon and Sunder. Subjects still made forecasts of future inflation, and the computer program continued to calculate the optimal savings amount conditional on the subjects’ forecast; subjects were instructed that the formula used by the computer program to determine savings decisions would “maximize your gain.” However, subjects were now free to experiment with the payoff implications of different inflation forecasts as well as to ignore the optimal-savings suggestion of the computer program when asked to state the fraction of their youthful endowment they wanted to save. In addition, they could consider information on the past savings decisions of other subjects. Another treatment variable concerned the money-creation process— whether the supply of money followed a constant exogenous growth process or was endogenously determined by the need to finance a fixed, real government deficit. Both money-supply rules give rise to two monetary equilibria, one involving a high inflation rate and the other involving a low inflation rate; the latter steady state is precisely the same under the two money-supply regimes. Under rational expectations the highinflation steady state is an attractor, but under first-order adaptive expectations, the lowinflation steady state is an attractor. Similar to the findings of Marimon and Sunder (1993, 1994, 1995), Bernasconi and Kirchkamp find that actual inflation converges to a neighborhood of the low-inflation monetary steady state under both monetary regimes, though inflation is systematically biased below the low-inflation steady state. The latter finding is consistent with the findings of Marimon and Sunder (1993, 1994, 1995). What differs is Bernasconi and Kirchkamp’s finding that savings under both regimes is greater than the optimal level (which is not possible in Marimon and Sunder’s design). Specifically, Bernasconi and Kirchkamp run a regression of actual individual savings choices ∗ . The results are reproduced in s ti on optimal choices as recommended to subjects, s i,t Table 1.4. As these results confirm, there is a significant difference between subjects’ actual savings choice and the optimal savings amount given their forecast. Bernasconi and Kirchkamp argue that a precautionary saving motive arising from subjects’ uncertainty regarding their inflation forecasts can rationalize the observed oversaving behavior. This finding would appear to invalidate the use of Marimon and Sunder’s “learning to forecast” experimental design; subjects do not make savings decisions as if they were

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Chapter 1 TABLE 1.4: Regression of actual savings on recommended, optimal savings. Source: Bernasconi and Kirchkamp (2000). s i,t

β

σβ

t-stat

Pr > |t|

95% Conf. Interval

∗ s i,t

1.015071

0.0012107

838.38

0.00

[1.012698, 1.017445]

certain of their forecasts of future inflation.29 Given that agents in macroeconomic models must (1) form rational expectations of future variables and (2) choose current quantities optimally in response to those expectations, further experimental work on this important topic is needed.30 Thus far, the experimental studies reviewed have considered environments where there is a single good, such as tickets, that is long lasting (durable); all other goods are perishable. If subjects perceive the unique durable good to be a store of value (perhaps owing to its durability), then that good necessarily serves as a medium of exchange, because it is the only good that can serve in that capacity. By contrast, experimental studies of the medium-of- exchange role of money are those which present subjects with multiple durable goods (candidates for money) and ask whether and which of these goods are adopted by subjects as money. Camera, Noussair, and Tucker (2003) consider the overlapping generations model with fiat money that we have just discussed and add to it a second store of value, an interest-bearing consol.31 The question addressed is whether fiat money continues to be used to transfer wealth from youth to old age when there is an interest-bearing and durable alternative. Understanding why money is used as a medium of exchange when it is dominated in rate of return by other assets is a critically important issue in monetary theory. Camera and others explore experimentally two complementary explanations for the rate-of-return dominance of fiat money. Their first, hoarding hypothesis— that assets bearing interest would be hoarded and not used as media of exchange when an alternative noninterest-bearing store of value exists—is tested by initializing the economy with stocks of both fiat money and consols but requiring that consols be traded predividend; that is, the dividend accrues to the owner of the consol after trading is completed. Their second, hysteresis hypothesis—that the old habit of using zero-interest fiat money dies hard—is tested by initializing a sequence of two-period overlapping- generations economies with a stock of fiat money that serves as the sole store of value and only later adding a stock of the interest-bearing consol, which trades either pre- or ex-dividend and seeing whether the fiat object continues to be used as a medium of exchange after the consol is introduced. Both these hypotheses are purely behavioral; the stationary rational-expectations equilibrium prediction in all treatments is that, in the presence of multiple stores of value, subjects will use the good offering the highest rate of return as a medium of exchange and eschew the other object. Consistent with the hysteresis hypothesis, the authors report that fiat money coexists with consols as a medium of exchange if there is a prior history of use of fiat objects alone as a medium of exchange. This coexistence is strongest when the consol dividend is paid after trade (consol is traded predividend) consistent with the hoarding hypothesis. If the consol dividend is paid after trade and consols and fiat objects are introduced simultaneously, then subjects cease to use the fiat object and exclusively use the consol as a medium of exchange.

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The use of money as a medium of exchange, even though it is dominated in rate of return by other stores of value, need not arise from irrational behavior. In the searchtheoretic approach to money as a medium of exchange, as pioneered by Diamond (1982) and Kiyotaki and Wright (1989) and extended by many others, equilibria can be derived in which durable goods that are not the least costly to store (have lowest return) can nevertheless serve as media of exchange under the belief that these goods will be more readily accepted in exchange by others, thereby reducing the time it takes an individual to acquire goods he or she wants to consume. A second virtue of the searchtheoretic approach over the models examined previously is that exchange of goods and money is decentralized and occurs via the bilateral trading decisions of anonymous, randomly matched agents, which is an altogether different friction than cash-in-advance or overlapping generations. This third mechanism giving rise to the use of money seems closer to what actually occurs in monetary economies than does a centralized market clearing mechanism. The predictions of the commodity money version of the Kiyotaki and Wright (1989) model are tested experimentally by Brown (1996) and Duffy and Ochs (1999). In this model, there are three goods (1, 2, 3) and equal numbers of three player types (1, 2, 3).32 Player type i desires to consume good i , which yields a per-period payoff of u, but type i produces good i + 1 modulo 3. Hence, there is an absence of a double coincidence of wants, and some players will have to trade for goods they do not desire to consume in order to obtain goods they do desire to consume; such goods may be regarded as commodity monies. Each player can store a single unit of a (perfectly durable) good in every period but pays a per-period storage cost c i . In the parameterization studied by Brown and Duffy and Ochs, c 1 < c 2 < c 3 . A trader starts out with a unit of his or her production good in storage. If he or she successfully trades for the consumption good, the trader gets the period payoff for consumption and then produces a unit of his or her production good, so the payoff is reduced by the cost of storing the good. Under one parameterization of the model studied by Duffy and Ochs, there exists an equilibrium where there is trade and all agents adhere to fundamental, storage-costminimizing strategies.33 For instance, type 2 players should trade their production good 2 with type 3 players in exchange for good 1, as this lowers type 2’s storage cost and reduces the time it takes type 2s to acquire their consumption good 2 via trades with type 1. The predicted pattern of exchange in the unique equilibrium is as shown in Figure 1.7. Under a different parameterization, the unique equilibrium prediction— also illustrated in Figure 1.7—calls for some player types to adopt speculative strategies, wherein they trade lower-storage-cost goods for higher-storage-cost goods, for example, type 1 players should agree to trade their production-good 2 with type 2 players for the more-costly-to-store good 3 as this reduces the time it takes type 1 to acquire its consumption good 1. This is a case where good 3 is used as a medium of exchange by type 1 even though it is dominated in rate of return (inverse of storage cost) by type 1’s production good 2. Brown tested only the speculative pattern of exchange and made use of a strategy method, wherein each subject stated his or her trading decision for all possible player types storing all possible goods prior to being randomly matched with a player; trades were then executed in accordance with strategies. Duffy and Ochs tested both sets of equilibrium-trading predictions. As in Brown’s study, subjects were assigned a fixed player type, but unlike in Brown’s study, following each random pairing with another player, subjects had to decide whether to trade the good they had in storage for the good of the other player; mutually agreed-upon exchanges were implemented. Despite these

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Pattern of exchange in the fundamental equilibrium

Pattern of exchange in the speculative equilibrium

Type 1

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Figure 1.7: Predicted trading patterns in the fundamental (left) and speculative (right) equilibria. In the fundamental equilibrium, type 2 trades good 3 to type 3 for the lowest storage cost, good 1, and then trades good 1 to type 1 for good 2. In the speculative equilibrium, an additional trade is predicted: type 1s agree to trade good 2 to type 2 for the more costly-to-store good 3 and then trade good 3 to type 3 for good 1. Goods 3 and 1 serve as media of exchange, though 3 is more costly. Source: Duffy (1998). TABLE 1.5: Frequencies of trade offers by the three player types, as reported by Brown (1996) and Duffy and Ochs (1999) in the speculative and fundamental equilibrium environments of the Kiyotaki and Wright (1989) model, along with equilibrium predictions. Speculative Parameterization Brown (1996) Duffy and Ochs (1999) Spec. Eq. prediction Fund. parameterization Duffy and Ochs (1999) Fund. Eq. prediction

Type 1 Trades 2 for 3

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differences, the experimental findings of the two studies are quite similar, as shown in Table 1.5, which reports the frequencies of exchange behavior in both the speculative and fundamental environments. The main finding of both studies is that, inconsistent with the theoretical predictions, subjects do not adopt the play of speculative strategies when such strategies constitute the unique equilibrium prediction. In particular, only around 13 of type 1 subjects storing good 2 agree to trade that good for the more costlyto-store good 3.34 In the environment where the fundamental equilibrium is unique, type 1s do not trade good 2 for good 3. However Duffy and Ochs report that trading decisions by type 1s in this environment are insignificantly different from decisions by type 1s in the speculative environment (see Table 1.5). Duffy and Ochs argue that subjects choose trading strategies based on immediate-past payoff experiences, as opposed to the more forward-looking marketability considerations that the theory emphasizes. In an effort to make marketability considerations more transparent to type 1 players, Duffy (2001) changed the distribution of the N subjects over the three types from 13 of each type to 13 of type 1, 29 of type 2, and 49 of type 3. Thus, type 1s were more likely to encounter a type 3 player and might therefore appreciate the use of the more costly-tostore good 3 as a medium of exchange. Indeed, Duffy (2001) reports an increase in the

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acceptance of good 3 by type 1 players from the 36% rate reported in Duffy and Ochs for the equal distribution of players across types to an acceptance frequency of 67% under the asymmetric distribution (still below the speculative frequency of 100%). Automating the decisions of type 2 and 3 players with robot traders who played fundamental trading strategies also helped to boost speculative trades by type 1 players to an average of 73%. These findings suggest that there exist certain parameterizations of the model in which a majority of subjects can learn to adopt speculative strategies where the money good is dominated in rate of return by other potential stores of value. All the goods in the search experiments just described had consumption value to one type of player. Duffy and Ochs (2002) add to this same environment an exogenous supply of a fourth good, 0, which is neither produced nor consumed by any player type. The question they pose is whether an intrinsically worthless, or “fiat object,” that is not invested with value by legal restriction would come to be used as a medium of exchange. Kiyotaki and Wright (1989) show that equilibria where this object is or is not traded coexist, so the issue is one of equilibrium selection. Duffy and Ochs’ (2002) experimental finding is that an intrinsically worthless fiat object will circulate as a medium of exchange so long as it has the lowest storage cost; if it is not the least costly to store good, that is, if it is dominated in rate-of-return, then its circulation as a medium of exchange is more limited than predicted by the theory. More recent generations of search-theoretic models of monetary exchange eliminate storage constraints, permit divisible exchanges of goods for money, and allow the money price of goods to be endogenously determined, as opposed to fixed rates of exchange; see, for example, the models of Shi (1995), Trejos and Wright (1995), and Lagos and Wright (2005). Versions of such environments have also been explored experimentally. For instance, Berentsen, McBride, and Rocheteau (2014) implement an economy with random bilateral matching to study how informational frictions concerning the “recognizability” of money affects bargaining outcomes between buyer/proposers and seller/producers. In particular, they study how private information by buyers regarding the redemption value of the type of money they offer to their matched producer (e.g., whether the money is counterfeit or not) or the amount of money (liquidity) they bring to a match matters for prices, the volume of exchange, and liquidity decisions. They report that, consistent with theoretical predictions, such adverse selection problems negatively impact prices, the exploitation of gains from trade, the acceptance of money as a medium of exchange and the liquidity positions of buyers. The Lagos and Wright (2005) model combines search-based models of money with competitive Walrasian equilibrium by appending a centralized market to the decentralized random-matching market. This construction enables agents to rebalance their money holdings each period, yielding a degenerate distribution for money holdings, a feature that makes the model tractable enough to do policy analysis. The addition of a centralized market, however, may mean that alternatives to money, such as trigger strategies, can be used to support social norms of nonmonetary “gift” exchange if the centralized meeting enables the detection of deviations from the social norm and the population of agents is finite. In such environments money may no longer be essential in the sense that the first best allocation is sustainable via community enforcement of the social norm of gift exchange (e.g., Kandori 1992; Araujo 2004; Aliprantis, Camera, and Puzzello 2007). Indeed, it is possible show in such environments that money may be inefficient relative to a social norm of pure gift exchange due to the delay between receipt of money and the ability to spend it (and the further possibility that money erodes in value due to inflation).

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Duffy and Puzzello (2014a) design an experiment to mimic the Lagos and Wright model with the aim of examining whether a social norm of gift exchange might emerge via a community-wide trigger-strategy mechanism and whether welfare is higher under this regime than a regime where exchanges of goods can be mediated by the exchange of an intrinsically worthless fiat object, which they call tokens. The experiment consists of a number of indefinite sequences, each consisting of a number of periods. Each period has two rounds, a decentralized round followed by a centralized round. In the decentralized round, agents are randomly paired and one member of each pair is assigned the role of consumer while the other is assigned the role of producer. The consumer moves first, proposing an amount of the match-specific good he or she would like the producer to produce. In the tokens treatment, the consumer can also offer the producer some of his or her tokens in exchange for the requested quantity of the good from the producer, though it is common knowledge that such tokens have no redemption value in the experiment. Production is costly to the producer in a linear fashion, while consumption is beneficial to the consumer, who has an induced concave utility function over units of the good consumed; the consumer’s utility gain from consumption always exceeds the producer’s linear cost of production over the feasible range. Producers either accept or reject the consumer’s proposal; if accepted, the proposal is implemented and if not, no exchange takes place. Following the decentralized round, all players meet in a centralized market where they can buy and sell a homogeneous good in exchange for tokens; the purpose of this centralized market is to allow rebalancing of subjects’ token balances. In the treatment without tokens, the centralized market is replaced by a simple public-good game, which permits signaling about the cooperativeness of agents in the economy (and thus maintenance of the social norm of pure gift exchange). Duffy and Puzzello report that in both treatments (tokens and no tokens), exchanges are accepted by producers about half the time; however, in the token treatment, the amount produced is about four times higher than in the no-token treatment. Duffy and Puzzello conclude that despite the possibility of higher welfare under a pure-gift-exchange equilibrium, the addition of tokens (money) results in higher welfare empirically; offering a token object in exchange for a costly-to-produce good serves to promote greater trust in impersonal exchange. Camera and Casari (2014) test a similar hypothesis, albeit in the context of a twoplayer, indefinitely repeated sequential-move prisoner’s dilemma game. Their main treatment variable is also the presence or absence of worthless “tickets” (money), which can be offered by the second mover to the first mover conditional (or unconditionally) on whether the first mover chooses the efficient “cooperative” action or the dominant “defection” choice (the second mover has no action choice). The first mover can play unconditional strategies or a conditional strategy of cooperation, provided that the second mover provides a ticket. They report that if subjects are not constrained by the number of tickets they have, the introduction of tickets leads to an increase in cooperative play relative to the treatment without tickets. The experiments of Duffy and Puzzello and Camera and Casari suggest an important mechanism by which cooperation can be sustained among anonymous, randomly matched strangers: the use of an intrinsically worthless token object.35 This “monetary” device is more commonly observed and used than other devices that experimentalists have tended to emphasize to date (e.g., costly punishment schemes or endogenous group-member selection) in the context of repeated gift-exchange or public-good games. Further experiments involving the Lagos-Wright environment include Anbarci, Dutu, and Feltovich (2013), who study the effect of an inflation tax by

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embedding Burdett, Shi, and Wright’s (2001) directed-search, price-posting model into a Lagos-Wright model of monetary exchange. They report that in their experiment—as in the model—inflation works as a tax because it reduces real prices, cash holdings, GDP and welfare. Moreover they find that the effect of the inflation tax on welfare is relatively greater at low levels of inflation than at higher levels. Duffy and Puzzello (2014b) study the effect of an unanticipated doubling or halving of the supply of money in a LagosWright model with money. Consistent with the neutrality–of–money proposition, they find no real effects from these changes to the money supply. Further, while prices roughly double with a doubling of the supply of money, they do not decline when the money supply is cut in half. Money’s third role as a unit of account is uncontroversial; prices are typically quoted in terms of money units and not in terms of (say) artichokes. However, as money typically depreciates in value over time due to inflation, most macroeconomic models presume that agents evaluate all choice variables in real terms, taking into account changes in the purchasing power of money. That is, they presume that agents are not subject to any kind of money illusion, defined as the failure to adjust nominal values for changes in prices.36 Experimental studies of money as a unit of account have sought to assess the extent to which individuals evaluate magnitudes in real terms or whether they are subject to some kind of money illusion. Motivated by survey evidence of money illusion (Shafir, Diamonds, and Tversky 1997) and on the downward stickiness of nominal prices and wages (Bewley 1999), Fehr and Tyran (2001, 2007, 2008) have conducted several experimental studies documenting money illusion and its consequences for nominal inertia. In the first of these studies, Fehr and Tyran have subjects play a four-player “price–setting” game. In each of 2T periods, each subject i chooses a price Pi and earns a real payoff that is a function of the time t average price chosen by other players, P−i,t , and the time t nominal money supply Mt : πi,t = f (Pi , P −i,t , Mt ) The function f yields a unique, dominance-solvable equilibrium for every value of M, is homogeneous of degree 0 in all arguments, and f P−i,t ≥ 0, so there is a weak strategic complementarity in price setting. In addition to treatments where subjects are paid according to this real payoff function, there is also a nominal payoff treatment, where subjects’ earnings are reported to them in nominal terms, P −i πi . Subjects are instructed on how they can deflate these payoffs into real terms by dividing by P −i . Fehr and Tyran characterize money illusion as a framing effect; behavior is predicted to differ depending on whether subjects are paid in real price adjusted terms, or in nominal terms. The difference comes in the adjustment to a nominal shock: the nominal money supply is known to be a constant level M for the first T periods and then to decline to a permanently lower level λM, λ < 1, for the last T periods. The issue addressed is whether subjects will adjust their prices downward at date T from P to λP , an adjustment that is more difficult in the nominal payoff function treatment, where subjects have to correctly deflate their nominal payoff function. A second difficulty, arising from the strategic complementarity in price setting, is that the failure of some subjects to adjust to the nominal shock may make it a best response for others who are not subject to money illusion to only partially adjust to the shock themselves. To eliminate the latter possibility, Fehr and Tyran conduct individual decision-making experiments under both the real and nominal payoff functions, where the other n − 1 players are known to the human subjects to be robot players who are not subject to

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Period Figure 1.8: The path of average prices in the four treatments of Fehr and Tyran (2001). The nominal shock occurs in period 0.

money illusion and who will adjust prices downward proportional to the shock and at the time of the shock. The experimental findings are nicely summarized in Figure 1.8, where we see that in three of the four treatments, the downward adjustment of prices to the new equilibrium occurs almost immediately following the fully anticipated reduction in M, whereas in the nominal payoff function with human opponents treatment, price adjustment is considerably more sluggish. Fehr and Tyran attribute behavior in the latter treatment to “the belief that there are subjects who take nominal payoffs as a proxy for real payoffs,” which leads those who hold those beliefs to adjust their prices more slowly. When the payoff function is presented in real terms or there are computerized opponents, such beliefs are unwarranted, and so the extent of price sluggishness is greatly diminished, if not perfectly eliminated. Fehr and Tyran further show that prices adjust more rapidly in response to a positive shock than they do in response to a negative shock. Petersen and Winn (2014) have replicated the main results of Fehr and Tyran (2001). They also find pronounced nominal inertia after a negative shock with a nominal payoff representation, and they confirm the presence of asymmetric effects after positive and negative shocks, as observed in Fehr and Tyran. However, Petersen and Winn also question aspects of Fehr and Tyran’s (2001) experimental design by pointing out that the slow adjustment in their nominal treatment with human subjects might not exclusively be belief driven but may also be driven by individual-level money illusion. Petersen and Winn design a new treatment, where they eliminate the coordination problem by

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having one subject play the role of all four price setters in Fehr and Tyran’s game. They report that prices also respond more slowly to a negative shock under a nominal than a real payoff representation, suggesting that individual-level money illusion plays an important role in this new decision situation (see Fehr and Tyran (2014) for a response and discussion). Fehr and Tyran (2007) consider a modified version of their price-setting game in which there are three Pareto-ranked equilibria. Unlike their prior experiment and that of Petersen and Winn, the focus here is not on adjustment to a shock but rather on equilibrium selection. In real terms, the ranking of payoffs associated with the three equilibria was π A > πC > π B , but in nominal terms, the ranking was: PC πC > P Aπ A > P B π B . The treatments were as in their earlier study: whether payoffs were presented in real or nominal terms and whether subjects played against n − 1 human or computer opponents. As before, subjects are instructed in how to deflate nominal payoffs into real terms. In the computerized treatments, the n − 1 robots play a best response to the past history of play of the human subject, effectively making the subject a Stackelberg leader. Fehr and Tyran’s main finding is that in the nominal treatment with human opponents, subjects coordinate on the inefficient C equilibrium, while in the real treatment with human opponents, they coordinate on the efficient A equilibrium; they interpret this as evidence of money illusion. In the nominal or real treatments with computerized opponents, with experience subjects get close to the efficient equilibrium, though not as close as in the real payoff treatment with human opponents; they attribute the latter to imitation of the choices of other human actors, as reflected in prices observed each period. In a third study, Fehr and Tyran (2008) consider not only the prior case, where there is a strategic complementarity in price setting, but now also consider the case where there is strategic substitutability in price setting, that is, f P−i,t ≤ 0. They report that money illusion and the resulting nominal inertia in response to a fully anticipated monetary shock is greatly reduced in the case of strategic substitutes relative to the case of strategic complements. In the strategic substitutes case, errors under adaptive learning are much greater following the money shock, leading to much faster adjustment toward more rational behavior than in the complements’ case. Thus, it appears important to consider the strategic environment in assessing the extent to which money illusion may matter for nominal inertia. Summing up, laboratory monetary experiments have examined whether individuals think in real or nominal terms and have explored the circumstances under which a token object can serve as a store of value as well as the characteristics of stores of value that make them more readily acceptable as media of exchange. While the experimental literature on monetary questions is one of the largest in experimental macroeconomics, there remains much further work to be done. For instance, most of the experimental studies of money we have discussed have fixed rates of exchange between money and goods, ignoring the important role of prices. Allowing for prices, one could then begin to think about exchange-rate determination between multiple money objects.37 While money illusion (together with the strategic environment) is an interesting explanation for nominal price stickiness, it is by no means the only explanation; indeed, most macroeconomists would point to other sources, including informational frictions, costly price or information adjustment, or staggered contracting. Experimental studies of the behavioral relevance of these other mechanisms is an important an open question for future research.

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4.2 Labor Economics Empirical research in labor economics typically involves the use of large-panel data sets as assembled by government agencies. However there is also a small and growing experimental literature that exploits the greater control and identification of causal relationships that is afforded by the laboratory relative to the field (e.g., Falk and Gächter 2008; Falk and Fehr 2003). Here I focus on some of the labor economic experiments that should be of interest to macroeconomists. An early experimental literature (previously reviewed by Camerer (1995)) examined individual behavior in intertemporal one-sided job-search models that are commonly used to study unemployment and labor-market policies (e.g., as surveyed by Mortensen (1987)). Experimental studies testing many of the comparative statics implications of job-search models include Braunstein and Schotter (1981, 1982), Hey (1987), Cox and Oaxaca (1989, 1992), and Harrison and Morgan (1990). For instance, Braunstein and Schotter (1981) test a number of theoretical hypotheses involving the one-sided model of intertemporal optimal job search with or without perfect recall. In this model, an unemployed worker draws a wage offer each period and must decide whether to accept or reject each offer, taking into account the known probability distribution of wage offers, search costs, and the level of unemployment compensation (if any). The optimal search strategy involves calculation of a reservation wage level; wage offers at or above this level are accepted and those below it are rejected. Braunstein and Schotter (1981, 1982) report experimental evidence in support of the notion that individuals choose reservation wages that are nearly optimal and accept or reject offers relative to this wage level. Among the treatment variables they consider are different wage-distribution functions, search costs, and whether subjects could recall past wage offers or faced uncertainty about the wage-distribution function they faced. Brown, Finn, and Schotter (2010) report experimental results from a continuoustime version of a labor search model where wage offers, w, are drawn randomly from a known distribution, F , arriving according to a known Poisson process with arrival rate λ. There is a continuous cost of delayed employment (job search), b, and payoffs are discounted according the instantaneous discount factor, ρ. Wage offers were received over a fixed interval of time and prior to seeing each offer, subjects were asked to state their reservation wage, such that if the arriving offer was greater than the stated reservation value, it would be automatically accepted. Once employed, no further search could occur for the duration of a two-minute sequence. In this simple, stationary environment, there is a unique reservation wage, w ∗ = w(F , λ, b, ρ), above which wage offers should be accepted and below which search should continue. In the experiment, subjects completed five consecutive search sequences (with lots of practice) over three different parameterizations of the model. The main experimental finding is that, counter to theory, in any given environment, subjects lowered their reservation wage over time, a phenomenon that is also observed in field analysis of how workers react to unemployment spells. To account for the collinearity between search time and accumulated search costs, they considered two additional treatments, one where subjects simply received job offers without any delay but with a random cost; in the other, the cost from remaining unemployed was set equal to zero, but the arrival of wage offers remained uncertain. Their results lead them to conclude that reservation wages decline over time primarily due to the uncertainty in the arrival of wage offers and not because of accumulated search costs.

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In addition to intertemporal labor-force-participation decisions, another labor market choice of interest to macroeconomists that has received some experimental attention is the labor-leisure trade-off. An increase in wages may have both substitution and income effects on hours worked. The impact of wage changes on labor supply is an important empirical question, as most business cycle models require the (compensated) elasticity of labor supply to be positive and sufficiently large so that transitory shocks can generate the large volatility in hours worked that is observed in macroeconomic data.38 Battalio, Green, and Kagel (1981) report experimental evidence confirming positive compensated wage effects on time spent working, though their experiments involved pigeons rather than human subjects. In particular, Battalio and others report that nearly all their hungry pigeons responded to a Slutsky-compensated wage decrease with a reduction in labor supply, which involved pecking a key. Using human subjects, Dickinson (1999) has experimentally examined two extensions to the classical labor-supply model. In the first, hours of work are no longer a choice variable but are instead fixed—a situation that characterizes many (short-run) employment relationships; indeed some business cycle theorists have exploited this type of nonconvexity as a means of increasing volatility in hours worked. However, in contrast to the standard theory, which assumes that workers provide full effort when on the job, Dickinson allows subjects to choose the intensity of their work effort; essentially they can decide whether to take on-the-job leisure. Specifically, subjects must participate in a two-hour experiment, during which time they are asked to type an unlimited supply of paragraphs, earning a fixed wage for every paragraph they type with no more than a few errors. The intensity of their work effort is examined in response to compensated changes in the (piece-rate) wage. Compensation was achieved by varying the value of nonlabor income. This kind of data on labor effort is typically unavailable to labor economists (who, at most, can observe labor hours) and serves to illustrate one of the advantages of studying labor market theories in the laboratory. In the second modification, subjects could choose both the hours worked—they did not have to stay for the duration of the two-hour experiment—and the intensity of their work effort, and these are again examined in response to compensated wage changes. In both the intensity and the combined intensity and choice-of-hours’ treatments, Dickinson reports that a majority of subjects, worked harder (less hard) when given a compensated wage increase (decrease); that is, the compensated elasticity of labor supply is, on average, positive. A notable feature of this experimental design, as well as that of Battalio, Green, and Kagel is that subjects really must choose to exert a level of effort at a task (pecking or typing) as opposed to experimental designs (discussed shortly) involving costly-but-effortless effort. More recently, experimental labor economics has moved in the direction of a more behavioral view of labor-market dynamics arising out of the influential work of Akerlof (1982) on efficiency wage theory (see also the papers in Akerlof and Yellen (1986) and Akerlof (2002)). While standard neoclassical theory presumes that, in a perfectly competitive equilibrium, all labor of a certain type is paid its marginal product, there is no involuntary unemployment, and, there are no problems of worker motivation, the efficiency wage theory disputes this view. In Akerlof’s (1982) original model, firms set wages above the competitive market level so as to better motivate employees; in exchange, employees’ effort levels are in excess of minimum standards so that the labor contract involves “partial gift exchange.” A consequence of setting nonmarket “efficiency wages” and the reciprocity by workers it induces is that fewer workers are

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Figure 1.9: Average observed effort as a function of wages. Source: Fehr, Kirchsteiger, and Riedl (1993).

hired than in competitive equilibrium, so some unemployment may be regarded as involuntary. The notion that labor-market contracts are incomplete—for example, on specification of effort levels or on the monitoring of effort or both, so that reciprocity in the form of gift exchange may play a role—has been tested experimentally in the form of the “gift-exchange game” first developed by Fehr and others (1993, 1998), with replications and variants subsequently studied by many others (see Gächter and Fehr (2002) for a survey of this literature or the chapter on other-regarding preferences by Cooper and Kagel (chapter 4)). The gift-exchange game is similar to a one-shot, sequential-move prisoner’s dilemma game or the trust game. All versions share similar features. In the original formulation of Fehr and others (1993), subjects are assigned roles as firms and workers and there are two stages to the game. In the first stage, firms post wage offers w ∈ [w, w], w < w, which may or may not be accepted by workers. Firms can employ only a single worker, workers can accept at most a single wage offer, and there are more workers than firms, so wage offers should be accepted immediately and should not exceed a worker’s reservation value; that is, all rents should accrue to the firm. If a worker accepts a wage offer, then in the second stage he or she has to choose an effort level, e ∈ [e e], e < e. Payoffs to workers are w − c(e), where c(e) is a convex cost of effort function, with the normalization that c(e) = w, which can be viewed as the workers’ reservation value. (Effort here is of the costly-but-effortless variety). Payoffs to firms are (v − w)e, where v is the firm’s redemption value. All payoff functions, wages, and cost-of-effort schedules were public knowledge. In the baseline model, workers and firms were separated and interactions were anonymous so that each two-stage game can be viewed as one shot; that is, reputational considerations cannot play a role. Thus, the subgame perfect-equilibrium prediction is that workers will choose the lowest possible effort level e; recognizing this, firms will offer the lowest possible wage w. The two-stage game is typically repeated ten to sixteen times. The main experimental finding, which has been replicated several times, is that workers reciprocate high wage offers with high effort. Figure 1.9 illustrates this main finding.

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In this figure, the competitive equilibrium (and lowest possible) wage w = 30, which is associated with minimum effort level e = 0.1. The maximum possible wage is 110 and the maximum effort level was 1. A wage of 30 was observed only once, and workers chose the minimum effort level only 16% of the time. The average wage was 72 and the average effort level was 0.4, both well above the competitive equilibrium predictions. Fehr and Falk (1999) modify the first stage of the gift-exchange game so that both firms and workers can propose and accept wage offers via a double auction, following the standard improvement rules. In the second stage, worker effort was either exogenously fixed by the experimenter, so that the contract negotiated in the first stage was “complete,” or workers were free to choose effort levels in the second stage, the case of “incomplete” wage contracts. As in the prior experiments, there were more workers than firms, so one would expect workers to underbid one another down to their minimum, reservation-wage levels. Fehr and Falk report two main findings. First, when contracts are completely specified by a wage offer (effort predetermined), this wage tends to be close to the competitive equilibrium level, where all rents accrue to the firm due to the smaller number of firms relative to workers. Second, when workers are free to choose effort levels, wages are significantly above competitive equilibrium levels, as in the earlier experiments where only firms could make wage offers. These higher wages are not because workers are refusing to undercut one another (a possibility suggested by Solow (1990)); Falk and Fehr report that there is, in fact, “massive underbidding” by workers seeking to secure wage offers. Interestingly, most firms refuse to accept these low-wage offers; while bid-improvement rules force workers’ wage offers to fall, firms are free to accept any wage offer and choose to contract only at wages well above workers’ reservation levels. Subjects in the role of firms recognize that subjects in the role of workers will provide greater effort the greater is the wage offered, and this recognition results in sticky, downward-wage rigidity. This evidence is consistent with survey evidence, for example, by Bewley (1999), indicating that managers recognize the impact of low wages on employee morale. In a third set of experiments, Fehr, Kirchsteiger, and Riedl (1996), Fehr, Gächter, and Kirchsteiger (1997), and Fehr and Gächter (2002) further modify the basic experimental design of Fehr, Kirchsteiger, and Riedl (1993) so that in the first stage, the wage contract specifies a wage, a desired effort level, and a fine for effort below the desired level. A third stage is added in which the worker’s effort level is probabilistically monitored by the experimenter; if below the desired level, the worker pays a fixed and publicly known fine to the firm. This design can be viewed as a version of Shapiro and Stiglitz’s (1984) deterrence-of-shirking version of the efficiency wage model, though in that model, a worker detected to be shirking is fired rather than fined. The issue explored in these experiments is whether the specification of desired effort levels, monitoring, and fines, that is, incentive contracting, undermines the positive reciprocity observed in experiments where these feature of the wage contract are unspecified. The results are somewhat mixed. On the one hand, firms are able to obtain effort levels above the requested level by setting high “efficiency wages,” as in the earlier experiments. On the other hand, firms tended to request too much effort and set wages too low to enforce a no-shirking outcome given the fines workers faced. Consequently, there is a substantial amount of shirking, despite the no-shirking-in-equilibrium prediction of the ShapiroStiglitz model. Among many other modifications to the experimental design of Fehr and others, Hannan, Kagel, and Moser (2002) are notable for allowing firms to be heterogeneous in their productivity levels. They test the hypothesis that workers might choose to

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supply lower effort at high-productivity firms and higher effort at low-productivity firms, all in exchange for high wages as in the latter case; the high wage of the low-productivity firm represents a larger gift to the worker by the firm. While they do not find evidence for such an effect, heterogeneity in firm productivity is a key characteristic of macroeconomic settings, and it is important to consider the impacts of such heterogeneity on wages and effort choice in the laboratory. Summarizing, experimental research pertaining to the labor market finds some support for the comparative statics implications of rational-choice job-search models and labor-leisure decisions. While that work focuses exclusively on labor-supply decisions, work by Fehr and associates has considered both labor demand and supply decisions. Consistent with efficiency wage theories, Fehr and associates have provided evidence that incomplete labor contracts and reciprocity concerns can lead to abovemarket clearing wages and involuntary unemployment. The collection of papers by Fehr and associates, in particular, is an excellent illustration of how a body of knowledge can be built up from a simple experimental game, to which additional features are incrementally added. The evidence provided in all these studies, for example, on the formation of reservation wages or the extent of involuntary unemployment, would be difficult to observe or identify outside the controlled environment of the laboratory. 4.3 International Economics A third sector of the macroeconomy in which experimental methods have been employed is the international sector. The justifications for an experimental approach to international economics are similar to those we have seen before: the available field data do not allow for precise tests of theoretical predictions nor is it possible to abstract away from complicating factors, such as transport costs or multilateral, as opposed to bilateral, two-country trade (most theoretical models assume the latter). Noussair, Plott, and Riezman (1995) conducted the first experimental test of two key principles of international trade: comparative advantage and factor price equalization. They consider two experimental environments involving eight to sixteen subjects each. The first is a labor-only, Ricardian model, and the second is one where both capital and labor are used as inputs into production.39 In both environments there are two countries and within each country, two player types: consumers and producers. Producers and consumers have induced desires to produce and consume quantities of the two goods Y and Z. In the Ricardian model, consumers inelastically supply labor L to producers for “francs” (money), which they use to buy quantities of the producers’ goods Y and Z. Producers use labor as input into production of goods Y and Z. There are equal numbers of consumers and producers in each country, and all subjects have the same endowments of labor and money. The two countries differ only in their production technologies: Country 1

Y1 = 3L 1

Z1 = L 1

Country 2

Y2 = L 2 ,

Z 2 = 2L 2

Thus country 1 (2) has a comparative advantage in the production of good Y (Z). While labor supplies, L 1 and L 2 , are not mobile across countries, trade in goods is possible, and there is no perceived difference in good Y (Z) produced by either country. Thus in the Ricardian model, there are six markets, two internal labor markets and four external

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goods markets for the two goods Y, Z produced by each of the two countries. These were implemented using computerized double auctions and induced values for inputs (by producers) and for goods bought (by consumers) and sold (by producers). The main hypothesis tested in this design is the law of comparative advantage; in the competitive equilibrium, trade occurs in the sense that members of two countries buy and sell goods Y and Z to one another, with county 1 completely specialized in the production (sales) of good Y and country 2 completely specialized in the production (sales) of good Z. This prediction may be contrasted with the inefficient autarkic outcome in which there is no trade between countries and, hence, no specialization. The second environment, which adds capital, differed in that the two countries had identical linear production technologies, that is, Y = L and Z = K in both countries, but different aggregate endowments of labor and capital and there was now an internal market for both labor and capital (both immobile factors). Thus this economy had eight markets. The main prediction of this environment is that both countries produced both goods and, in the competitive equilibrium, country 1 would be a net exporter of good Y and country 2 a net exporter of good Z. Further, in the competitive equilibrium, prices of the two goods should be equalized across countries, and this further implies factor price equalization. Such equalization does not occur under autarky. The experimental results are somewhat mixed. On one hand, there is strong support for the law of comparative advantage; in the Ricardian environment there is nearly complete specialization by producers in the two countries, and in the environment with capital, the two countries’ net exports are of the good for which they hold a comparative advantage. Further, in the environment with capital, output prices are equalized across countries and given the identical linear production functions so are factor prices. The latter finding is one that would be very difficult to observe outside of the controlled environment of the laboratory as it holds only in special cases such as the one induced here. On the other hand, input and output prices are neither consistent with competitive equilibrium or with autarkic levels. Noussair and others argue that production and consumption patterns appear to be converging toward competitive equilibrium levels, especially under free trade (they also consider some environments with tariffs). As evidence for convergence, they make use of regression equations of the type (1) discussed in Section 2.1. In a related paper, Noussair, Plott, and Riezman (1997) focus on issues of international finance: exchange-rate determination, the law of one price, and purchasing power parity. They simplify the setup from their prior experiment so that there are no longer any factor inputs or production processes; there is simply an endowment of two final goods X and Y in each of the two countries, A and B. A further difference is that each country now has its own money. Each country was populated by six subjects, three of whom were sellers of (endowed with) good X and buyers of good Y and the other three were sellers of (endowed with) good Y and buyers of good X. In addition subjects were endowed with amounts of their home currency only. As in the prior study, a demander of good X was indifferent between acquiring X from a supplier in his or her home country or in the foreign country. However, foreign country purchases required acquisition (cash) in advance of the foreign currency. A further restriction designed to force the use of currency markets was that residents of one country could not transport and sell goods abroad so as to obtain foreign currency for purchases abroad. (On the other hand, goods purchased abroad could be costlessly transported home). In each country, markets in the two goods and foreign currency were implemented using computerized double auctions. Subjects were induced to value quantities of goods X

•

Chapter 1 60

50

Exchange rate

52

Competitive equilibrium

40

30

20

011393 011493 040793 042193

10

0

1

2

3

4

5

6

7

8

9

10

Period Figure 1.10: Mean exchange rate of currency A for currency B over ten trading periods of the four sessions of Noussair, Plott, and Riezman (1997). The competitive equilibrium prediction is an exchange rate of 47.

or Y and the home currency only; the end-of-session redemption value of any foreign currency holdings was zero. The exchange rate e—the price of currency A in terms of currency B—is determined according to the balance-of-payments approach, wherein e equates the demand and supply for currencies A and B arising out of the flow of international transactions, as predicted by comparative advantage: in the competitive equilibrium, country A (B) is an importer of good X (Y). Given this balance-of-payments view and supposing that trade occurs, the main hypothesis tested concerns the law of one price: e P XA = P XB

e PYA = PYB

That is, adjusting for exchange rates, goods X and Y have a single world price. The alternative hypothesis is again that the inefficient, autarkic, no-trade outcome is realized, in which case the law of one price does not hold. The experimental findings are somewhat mixed, though the authors conclude that their data are closer to the competitive equilibrium than to the autarkic predictions, again using regression equations of type (1). On the one hand, they find somewhat remarkable (given the complexity of the environment) evidence of convergences to the competitive equilibrium exchange rate prediction e = 47 across four sessions, as shown in Figure 1.10. On the other hand, the law of one price (and a variant, purchasing-power parity that is based on price level indices) fails to obtain. Noussair, Plott, and Riezman (1997) conjecture that this failure arises because of different speeds of convergence of prices in the two domestic markets, which leads to a failure of the law of one price, even though the exchange rate is at the competitive equilibrium level. Increasing the duration of the experiment beyond the ten fifteen-minute trading periods in a session might have allowed for such a convergence to take place.

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One observation regarding this pair of experiments is that the autarkic outcome, while soundly rejected, is something of a straw man; absent restrictions on trade, the notrade outcome does not comprise an equilibrium and is rationalized as being plausible if subjects are so averse to foreign-exchange-market uncertainty that they refuse to engage in trade. Nevertheless, the important value of these experiments in illustrating how basic tenets of international trade and finance can be tested in the laboratory cannot be emphasized enough, and much further work could be done along these same lines for example, allowing capital flows across countries. Some theoretical work on exchange-rate determination is in environments where there are no restrictions on portfolio holdings and the demands for currencies are endogenously derived, as opposed to the cash-in-advance-induced demand for currency in the design of Noussair, Plott, and Riezman (1997). In this more general environment, if two monies are perfect substitutes and there is no government intervention in currency markets or legal restrictions on currency holdings, the exchange rate may be indeterminate. Further, if agents have perfect foresight, it is predicted that whatever the exchange rate turns out to be, it will be invariant over time, as in the overlapping generations model of Kareken and Wallace (1981). These two predictions are tested in an experiment by Arifovic (1996) that was designed for comparison with the predictions of an agent-based model (a genetic algorithm). In the experiment there was a single consumption good and equal, fixed supplies of two currencies, francs and lire. As the environment is an overlapping generations model, even- or odd-numbered subjects alternated every even/odd period between being young and receiving endowment ω y of the consumption good and being old and receiving endowment ωo of the consumption good, with ω y > ωo . They were then reborn as young agents, repeating the two-period cycle of life anew. Subjects were induced to hold log preferences over consumption in the two periods of life, so their optimal plan involves consumption smoothing, or selling some of their endowment for the two monies (the only stores of value) when young and redeeming these money holdings in the next period at prevailing prices for old-age consumption. Initial-period old subjects were endowed with equal amounts of the ten units of the two currencies. Each young subject was called on to make two decisions: how much of their youthful endowment to save (the remainder was consumed) and what fraction of their savings was to be held in domestic currency; the remainder was placed in foreign currency holdings. Old subjects inelastically supplied their money holdings for consumption. The exchange rate between the two currencies was that which equated youthful demands for, and old agent supplies of the two currencies. The main experimental finding was that the mean exchange rate was about 1, but counter to the stationary perfect-foresight equilibrium prediction, there were persistent fluctuations in the exchange rate. Arifovic attributes this volatility to small changes in the portfolio decisions of young agents in response to immediate past differences in rates of return on the two currencies, which in turn generates volatility in the exchange rate in a continual feedback loop. Observed volatility in exchange rates has been difficult to explain—many attribute it to “news” or “sunspots”—but Arifovic’s experimental finding of adaptive learning dynamics with regard to portfolio decisions provides a new alternative. Fisher (2001) revisits the issue of the law of one price and purchasing power parity that Noussair and associates failed to observe in their experiment by constructing a greatly simplified, version of the Noussair, Plott, and Riezman (1997) environment. In Fisher’s design, each country produces only a single good, the prices and supplies of which are perfectly controlled by the experimenter, so the main job of subjects

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(as in Arifovic (1996)) is to determine the nominal exchange rate. The two goods and currencies are green (domestic) and red (foreign), and green (red) currency is required in advance to buy green (red) goods (so, this is again the case of a cash-in-advanceinduced demand for currency). Each subject begins a session endowed only with a large supply of the green currency.40 The price and end-of-session redemption value of a unit of the green good, p g and v g , are fixed and known for the duration of a session, as are the end-of-session redemption value of a unit of the red good, vr , and the green currency. Red currency is in limited supply, has no end-of-session redemption value, and cannot be carried over from one period to the next; its main purpose is to purchase the red good. The red currency price of a unit of the red good in period t, ptr —a treatment variable— is randomly determined from a set of values and announced at the beginning of each of the ten periods that comprise a session. Supplies of the two goods are unlimited, but vr > v g , which motivates a demand for the red good and red currency. The limited supply of red currency each period, equal to just k − 2 units, where k is the number of subjects, is held by the experimenter. After the unit price of the red good for the period ( ptr ) is announced, the supply of red currency is auctioned off in a second-price, sealedbid auction. Each subject could bid amounts of green currency for just one of k − 2 units of red currency during this first auction phase of a period. The market-clearing price of a unit of red (foreign) currency in terms of green (domestic) currency (equal to the second-lowest bid submitted) is interpreted as the nominal exchange rate for period t, e t . Once e t is determined, subjects were free to buy units of green and red goods subject to cash-in-advance and budget constraints. Fisher’s main hypothesis—a relative version of purchasing power parity—is that the real exchange rate in each period t, defined by qt = e t ptr / p g , is invariant over time, that is, that the market clearing, nominal exchange rate e t immediately adjusts to the announced red good prices, ptr , so as to keep the real rate, qt , constant. A related hypothesis, absolute purchasing power parity, posits that the real exchange rate qt equals vr /v g , the marginal rate of substitution between foreign and domestic goods, so the nominal exchange rate in each period is determined according to et =

vr p g v g ptr

Thus Fisher’s exchange-rate-determination process arises out of purchasing-power parity, as opposed to the balance-of-payments approach to exchange-rate determination followed by Noussair and others, which relies on trade flows between countries. With this stripped-down experimental design involving perfectly controlled prices, Fisher finds convincing evidence for both the relative and absolute versions of purchasingpower parity. This finding confirms a conjecture of Noussair and others that the failure of purchasing-power parity in their study was likely owing to the slow and differential convergence of prices in the goods markets; in Fisher’s design there is no problem with nonconvergence of goods prices as these are predetermined. Fisher also adds an interest rate to red currency holdings over a subperiod of each period as well as uncertainty regarding the price of the red good in order to test hypotheses related to covered and uncovered interest parity. He finds support for these hypotheses as well. Having studied a greatly simplified exchange rate environment, Fisher (2005), in a follow-up paper, seeks to understand two complicating factors that might account for the widespread lack of evidence in support of purchasing power parity and (un)covered interest parity in econometric analyses of historical field data.41 He considers the role of

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(1) nontraded goods, which if sizeable, may lead to failures of purchasing power parity in analyses using aggregate price indices, and (2) nonstationary price-level dynamics. Proxies for these two complicating factors are introduced into the design of Fisher (2001). Prices for both nontraded goods and nonstationary goods are found to increase the deviation of exchange rates from theoretical predictions, with the largest deviations coming from the environment with nonstationary prices. Menzies and Zizzo (2012) also use laboratory experiments to study exchangerate determination. They implement a model where exchange rates are determined by financial flows (as opposed to real factors), focusing on the impact of monetary shocks for exchange-rate determination in nonstochastic and stochastic versions of their model where covered—or, respectively, uncovered—interest parity holds in the steady state. They find that in their nonstochastic model, where the only shock is to the money supply, exchange rates largely follow covered interest rate parity predictions, especially among experienced subjects (who are brought back to participate in the same experiment again). However in their stochastic model, where in addition to the moneysupply shock, there are two additional shocks, a money-demand shock and a moneymeasurement shock, they find that there is a substantial downward bias in exchange rate movements (“conservatism”) relative to uncovered interest rate parity predictions even among highly experienced subjects—a finding that accords with numerous empirical studies using field data. Summarizing, the laboratory has been used to test some basic principles of international economics, including the law of comparative advantage, the law of one price, purchasing-power parity, and theories of exchange-rate determination. These are phenomena that are either difficult to test (comparative advantage) or explain (exchange rate volatility) or which have been refuted in econometric tests with available field data (purchasing-power parity, uncovered interest-rate parity). We have seen how experimental methods can shed light on these topics and how building on prior experimental designs can help to clarify puzzling findings, such as Noussair and others’ finding that purchasing-power parity does not hold. Further work on this topic might consider adding dynamic, intertemporal linkages such as would occur by adding capital accumulation or considering intertemporal consumption savings/decisions. One shortcoming of the international experiments reported on here is that in many (but not all— e.g., Fisher (2005) and Menzies and Zizzo (2012)) cases, the number of experimental sessions of a treatment are too few. In implementing complex international economic environments, the temptation is to load up each session with many changes in treatment variables, a practice that is understandable but one that should be avoided nonetheless. 4.4 Multisectoral Macroeconomics A few courageous researchers (namely, Charles Plott and associates) have sought to combine all three of the sectors we have explored in the last few sections by implementing large-scale laboratory macroeconomies. Such multisectoral systems, involving simultaneous markets for factor inputs, goods, and money as well as foreign goods and money, may be what many people have in mind when they hear the term macroeconomic experiments. I hope it is clear by now that a macroeconomic experiment need not be elephantine; rather it suffices that the experiment addresses a topic of interest to macroeconomists. Nevertheless, it is of interest to understand the extent to which many interlinked experimental markets can operate simultaneously in order to identify the source of inefficiencies.

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A first effort at developing such a multisectoral laboratory macroeconomy is found in Lian and Plott (1998), who implement a static, Walrasian competitive general equilibrium model. There are two types of agents, consumers and producers, two goods, X and Y, and a constant supply of fiat money. Consumers were induced to have a preference function U (X, Y) over the two goods. Each period they were endowed with zero units of X and a constant amount of Y; X can be interpreted as a consumption good and Y as labor/leisure. Producers desired good Y only and could consume it directly (e.g., labor services) or use it as input into production. Producers were endowed with a concave, labor-only production technology yielding f (Y) amount of good X for Y units of input. Producers were endowed with an amount of fiat money and good X in the first period only; these endowments were not refreshed in subsequent periods (e.g. a constant money supply). In simultaneously operating, multiunit double auctions, consumers could trade good Y with producers for fiat money, and consumers could purchase good X from producers in exchange for fiat money—that is, a cashin-advance constraint was binding. Units of X or Y that were consumed/used as input into production left the system (subjects received redemption values for these based on their induced utility/production functions). Somewhat strangely, remaining balances of X and Y were carried forward to the next period, investing consumption and labor with a durability—and asset value—that they would not ordinarily possess (and which would have obviated the need for fiat money, absent cash-in-advance constraints). Finally, all subjects (producers and consumers) had access to a financial market where they could borrow and lend to one another in fiat-money-denominated contracts through a one-period bond market. Default was discouraged through the use of large exogenous fines. Given the initial cash endowments, in the static competitive equilibrium resulting from consumer and producer optimization, there are no cash constraints and financial markets should not operate. However, there is a unique equilibrium volume of production and consumption of goods and ratio of the price of a unit of Y to a unit of X that is independent of the number of subjects. Each session consisted of a number of periods. The final period was not announced in advance; market prices during that final period were used to evaluate final inventory holdings which were redeemed into cash at a fixed rate. The economy is illustrated in Figure 1.11, which also gives the induced utility and production functions used in the study. Subjects for this study were nontraditional, consisting primarily of high school students participating in a summer school program at Caltech. In addition, one session involved science and engineering graduate students from the People’s Republic of China. Aside from these different subject populations, the main treatment variables were variations in the exogenous money supply and the experience level of subjects (whether they participated in more than one session). Among the main findings, Lian and Plott (1998) provide convincing evidence that there is considerable order to the observed economic activity. Using regression equations of form (1), they show that convergence toward the competitive equilibrium outcome appears to be occurring, albeit slowly; indeed, they formally reject the hypothesis that the competitive equilibrium is actually achieved. Still, the ratio of the price of Y to the price of X, predicted to be 2, is found to be around this level in all sessions. Volume in both the input and output markets is only slightly less than predicted, and this is attributed to overconsumption of Y by consumers and underproduction of X by producers, who also overconsumed Y. Financial markets are rarely used as predicted. Experience is shown to matter greatly in reducing the volatility of prices and volume

Experiments in Macroeconomics

X production X = 6Yp – Yp2

Payoff = U(Yc) $ = 170Yc – 10Yc2

X inventory

X inventory

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57

X consumption

X market

Francs

Financial market

Francs

Cash

Mid bond

Cash

End bond

Payoff = U(Xc,Yc) $ = 72Xc – ½Xc2 + 320Yc – 16Yc2 – 1600

Y market Y consumption

Y inventory

Y inventory

Y consumption

Initial endowment

Figure 1.11: Circular-flow model illustrating the experimental environment of Liam and Plott (1998).

and improving efficiency. Changes in the money supply have proportionate effects on the price level but no real effects, and the velocity of circulation of money appears to hit a constant level, especially with experience. Perhaps the most intriguing findings are based on constructed measures of unemployment, inflation, and real GNP. Using these, Lian and Plott (1) find no evidence for any inflation-output Phillips-curve-type trade-off, and (2) strong support for a negative trade-off between changes in the unemployment rate and changes in real GDP (a version of Okun’s law).42 With a keen knowledge of how their macroeconomy operates, Lian and Plott interpret the latter phenomenon as “no surprise. . . , A fall in unemployment translates to an increase in system efficiency and that becomes an increase in income and thus real GNP” (p. 62). Building on Lian and Plott (1998) as well as Noussair, Plott, and Riezman (1995, 1997), Noussair, Plott, and Riezman (2007) develop an experimental multisectoral macroeconomy, which they claim (p. 50) is “far more complex than any laboratory economies created to date.” This claim cannot be disputed. The economy has three output goods, x, y, and z, and two factor inputs, labor l and capital k, all of which are specific to one of three countries, A, B and C, each of which has their own currency, a, b, or c. Thus there are twenty-one double auction markets in simultaneous operation, seven markets in each country—the three goods markets, the two input markets and two currency markets. Three experimental sessions were conducted, each involving in excess of fifty subjects; two of the three experiments were conducted remotely via the Internet. The subjects were divided up roughly equally into twelve types, with each type being characterized by a country of residence and typically assigned two of three possible roles: as a producer of output goods, consumer of two output goods, or supplier of input goods. The precise roles of each subject type, the (continuous) induced production function f (k, l ), utility function over the two goods U (·, ·), and/or supply of input cost function C (k, l ) are given in Table 1.6.

Country

A

A

A

A

B

B

B

B

C

C

C C

Type

1

2

3

4

5

6

7

8

9

10

11 12

Producer of x Consumer of y Producer of y Consumer of x and z Producer of z Consumer of x and y Supplier of l and k Consumer of z Producer of y Consumer of y and z Producer of y Consumer of x Producer of z Consumer of x and y Supplier of l and k Consumer of z Producer of x Consumer of y and z Producer of y Consumer of x and z Producer of z Supplier of l and k Consumer of x and y

Role f xA (k, l ) = 4l 0.25 k 0.25 U (y) = 1650y−100y 2 f yA (k, l ) = 2l 0.25 k 0.25 U (x, z) = 700x − 100x 2 + 1900z − 100z2 f zA (k, l ) = 2l 0.25 k 0.25 U (x, y) = 700x − 100x 2 + 1650y − 100y 2 C (l , k) = 26l + 2l 2 + 10k + 5k 2 U (z) = 1900z − 100z2 f xB (k, l) = 2l 0.25 k 0.25 U (y, z) = 3900y − 400y 2 + 5600z − 400z2 f yB (k, l) = 4l 0.25 k 0.25 U (x) = 3800x − 400x 2 f zB (k, l) = 2l 0.25 k 0.25 U (x, y) = 3800x − 400x 2 + 3900y − 400y 2 C (l , k) = 48l + 15l 2 + 55k + 7.5k 2 U (z) = 5600z − 400z2 f xC (k, l) = 2l 0.25 k 0.25 U (y, z) = 13500y − 1000y 2 + 16000z − 1000z2 f yC (k, l) = 2l 0.25 k 0.25 U (x, z) = 12000x − 1000x 2 + 16000z − 1000z2 f zC (k, l) = 4l 0.25 k 0.25 C (l, k) = 300l + 50l 2 + 220k + 20k 2 U (x, y) = 12000x − 1000x 2 + 13500y − 1000y 2

Parameter Values

5 5

5

5

5

5

5

5

5

5

5

5

No. in exp 1

2 3

3

4

4

4

4

4

3

3

3

3

No. in exp 2

4 5

5

5

5

4

5

5

5

4

5

5

No. in exp 3

TABLE 1.6: Twelve subject types, preferences, cost, and production functions and the numbers of each type in the three sessions of Noussair, Plott, and Riezman (2007).

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The actual functions were discretized and presented to subjects as tables. Using the induced functions in Table 1.6, aggregate demand and supply functions can be calculated. From these equations, the competitive equilibrium can be found using fifteen market clearing conditions for output and input markets, together with three lawof-one-price (no arbitrage) conditions and three flow-of-funds equations determining exchange rates. Countries A, B, and C have a comparative and absolute advantage in x, y, z, respectively. As in Noussair, Plott, and Riezman (1997), the main comparison is between the efficient, full-trade, competitive equilibrium prediction and the autarkic, no-trade outcome. The main difference between Noussair, Plott, and Riezman (2007) and Noussair, Plott, and Riezman (1997) is the addition in the former of factor input markets for labor and capital. In essence, the Noussair, Plott, and Riezman (2007) environment is a combination of Noussair, Plott, and Riezman (1995) and (1997) with a third country added and a proportionate increase in the number of subjects. What is the motivation for such an exercise? As in Lian and Plott (1998), it is to demonstrate that such an experiment is possible, and that competitive equilibrium remains an attractor despite the complexity of the environment. As the authors themselves say: The number of [excess demand] equations explodes as the number of commodities and resources increase, but theory itself suggests no effects of the increased complexity. On the surface, the thought that a decentralized system of competitively interacting humans might approximate the [competitive equilibrium] solution as the number of equations grows large is a staggering and contentious proposition that many cannot believe without demonstration (Noussair, Plott, and Riezman 2007, p. 50).

The main finding of Noussair, Plott, and Riezman (2007) is again that the most prices, wages, exchange rates, production, consumption and trade volumes are closer to the competitive equilibrium prediction than to the autarkic outcome, again using regression equations of the form of equation (1). In this study, however, the pattern is less obvious than in the simpler economies of Lian and Plott (1998) and Noussair, Plott, and Riezman (1995, 1997), perhaps reflecting the additional complexity of this environment. Among other new findings, there appears to be much more pronounced “home bias,” in the sense that imports are considerably lower than competitive equilibrium levels. Further, price volatility is greatest in exchange rates, intermediate for producer (input), prices, and lowest for output prices. Interestingly, Noussair and others attribute these findings to less than complete equilibration as opposed to the more traditional view that markets are in equilibrium and institutional factors, government policies or exogenous shocks are responsible for any observed inefficiencies or volatility. Somewhat simpler, though perhaps clearer, multisector macroeconomic experiments involving just one input (labor) and one output (good) market have been conducted by Bosch-Domènech and Silvestre (1997) and Roos and Luhan (2008). Bosch-Domènech and Silvestre (1997) consider a general equilibrium economy with subjects playing the role of worker/consumers and producers. Consumers have endowments of labor available at the start of each period and endowments of nonlabor income received at the end of each period. During a period they can sell labor to firms for an experimental currency and use the proceeds to buy the firms’ output. In addition, they can borrow a fraction r of their end-of-period endowment of nonlabor income to finance their purchases of the firm output. However, any use of credit to make purchases must be repaid at the end of each period out of the known

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end-of-period nonlabor income endowment (this is a static model with no carryover of debt). Further, there are periodic variations in the value of r , the credit constraint, which serves as the main treatment variable. Consumer-workers seek to maximize the utility of their consumption of the firms’ good less their disutility from supplying firms with labor. Producers are endowed with a common (labor-only) production function and are paid on the basis of profit maximization alone. Thus, consumer-workers sell labor and buy output while firms buy labor input and sell output. Double auctions are used for both input and output markets. Interestingly, there is no sequencing as to when labor and output markets are open; consistent with the theory, they are both open simultaneously. Nevertheless, Bosch-Domènech and Silvestre report that input trades occur in the first part of each period, followed by output trades, a rather natural order. Their main finding is that variation in credit-market conditions matters for both prices and transactions. For values of r below a critical level r ∗ , corresponding to tight credit-market conditions, both prices and transactions are predicted to increase with r . However, above this limit, the credit-market-restriction is no longer binding on the unique competitive equilibrium allocation (given the preferences and technology), and so prices and transactions should stabilize at competitive equilibrium levels. The experimental results are largely in accordance with these theoretical predictions; with tight credit-market conditions, prices and transaction volume are well below the unconstrained competitive equilibrium predictions and rise as r is increased. However, for sufficiently loose credit-market conditions, that is, r > r ∗ , variations in the creditmarket constraint have no effect on prices and transaction volume, which remain at competitive equilibrium levels. This is the first and only experiment that provides evidence of the impact of credit-market constraints in a general equilibrium setup. Other studies such as Lian and Plott (1998) focus on variations in the money supply and not credit. Roos and Luhan (2008) also consider a macroeconomy with a single input and output market but with explicit sequencing: unionized workers move first, setting their nominal wage, followed by firms who buy labor input and produce output. Finally, the price level is determined by equating an exogenously given (but unknown) market demand with the output supplied by all firms. Differently from the other multisectoral studies, Luhan and Roos examine both the real wages, labor demand, and prices that result from subjects’ choices as well as expectations of market prices, which they elicit from subjects. They report that both firms and workers engage in “imperfect optimization,” given their expectations. Nevertheless firms come close to maximizing their profits, while workers who move first and thus face greater uncertainty than firms, generally set wages too high given their price-level expectations. The construction of such multisectoral macroeconomies to study the predictions of static, competitive general equilibrium theory is an important achievement. Further work along these same lines might seek to incorporate more intertemporal, forwardlooking behavior, in which expectations of future variables determine current quantities as in much of modern, dynamic macroeconomic modeling. Of course, a difficulty with this research agenda is that the systems studied are so complex to analyze, not to mention logistically difficult and costly to implement, that other researchers may be discouraged from following up with the crucial replication and extension studies that are essential to scientific progress. Perhaps as computing, coordination, and recruitment costs decline further with further innovations in social networking technology, multisectoral macroeconomic experiments of the scale pioneered by the authors mentioned here will become more commonplace.

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5 MACROECONOMIC POLICIES As we have seen, many researchers have felt confident that they could test the predictions of modern, microfounded macroeconomic models in the small scale of the laboratory. It should not be surprising, then, to find that several researchers have also used the laboratory to examine the effects of macroeconomic policies. As such experimentation is not typically feasible (not to mention ethical) for macro policymakers, the laboratory provides an important and (to my mind) underutilized environment in which to assess the likely impact of macroeconomic policies before such policies are actually implemented. 5.1 Ricardian Equivalence One important macroeconomic policy debate to which experimentalists have contributed concerns whether a temporary fiscal stimulus, financed by government borrowing, is preferred to a tax-financed stimulus or, as Barro (1974) put it, whether government debt is viewed as net wealth. In Barro’s reformulation of the Ricardian equivalence doctrine, given an operational intergenerational bequest motive, lump-sum taxes, perfect capital markets, and no change in government purchases, the timing of tax levies (now or later) is irrelevant. An issue of government debt to finance temporary spending is readily absorbed by the public, who perfectly anticipate using these bond holdings to pay for the necessary future increase in taxes, thus leaving all real variables—for example, output and interest rates—unaffected. Thus, the consequences of a bond or tax-financed stimulus are equivalent: there are no real effects. The empirical evidence using field data on whether Ricardian equivalence holds or not is mixed (for contrasting conclusions, see Bernheim (1997) and Seater (1993)). However the environment in which the Ricardian doctrine holds—for example, lump-sum taxes, strong intergenerational bequest motive, and so on—is not one that is necessarily observed in nature. For this reason, the laboratory may be the more desirable place in which to explore the question of Ricardian equivalence; indeed, several experimental studies have directly addressed this question. Cadsby and Frank (1991) design an experiment that closely mimics the overlapping generations model that Barro (1974) used to formalize the notion of Ricardian equivalence. In Cadsby and Frank’s design, an experimental session involves eight to ten rounds, with each round consisting of three periods, labeled as periods A, B, and C. At the start each session, subjects were anonymously paired. Within each pair, one member played the role of generation 1 while the other played the role of generation 2. Pairings and roles were fixed for all rounds of a session. Subjects were endowed with tokens in various periods, and these could be converted into certificates (consumption) at a price of 1 token = 1 certificate, or tokens could be stored for future periods (savings). Members of generation 1 make consumption and savings decisions in period A, denoted by C 1A, S1A, and also in period B, denoted by C 1B , S1B , and are inactive in period C. The savings of generation 1 in period B, S1B , which is constrained to be nonnegative, is given as a bequest to their generation 2 partner and is available to that partner at the start of period C. A bequest motive for members of generation 1 was induced by the choice of preferences (as illustrated shortly). Members of generation 2 have no bequest motives— they can be viewed as the descendents of generation 1—and are inactive (unborn) in period A. Those in generation 2 also make consumption and savings decisions in period B, denoted C 2B , S2B ; they do this knowing the amount of any tax they will face

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in the final period C. In period C, the remaining savings of generation 2, including bequests received, S1B , from generation 1, are consumed (converted into certificates). After period C ends, the round is complete and if the last round has not been played, a new round begins following the same sequence of choices and refreshed endowments. The main treatment variables consisted of the token endowments generations 1 and 2 received in periods A and B and the amount of deficit spending (the tax burden) generation 1 received in period B and generation 2 was required to repay in period C. There was also some variation in the induced preference functions, with a multiplicative utility function performing better than an additive one. The hypotheses concerned the amounts consumed, saved and bequeathed in response to temporary expansionary and contractionary government policies. To simplify the environment as much as possible, there was neither discounting nor interest payments on government debt. Here I will describe one experiment, number 3, that seems representative of Cadsby and Frank’s experimental design and findings. In this experiment, generation 1 agents’ induced utility function was of the multiplicative form, U1 (C 1A, C 1B , U2 ) = C 1AC 1B U2 , and included as an argument the utility of generation 2, which was given by U2 (C 2B , C 2C ) = C 2B C 2C ; this was the manner in which a bequest motive was operationalized. Notice both agent types should seek to intertemporally smooth consumption and in that regard, the experiment can be viewed as another test of intertemporal optimization (as discussed at the beginning of this chapter), albeit now with a bequest motive added. In years 1–5, generation 1 received token endowment E 1A in period A and 0 in period B, while generation 2 received token endowment E 2B in period B and 0 in period C. In years 6–10, generation 1 received endowment E 1A in period A as before but now received an additional token endowment in period B of E 1B > 0. The latter is viewed as temporary deficit spending. Generation 2 received endowments of E 2B in period B as before but now had to pay a tax out of accumulated savings at the start of period C equivalent to E 2B , an amount that was precisely equal to the amount of his or her parent’s period B endowment. Under perfect foresight, the optimal consumption/savings plan is derived by solving generation 2’s problem first: max

S2B ,C 2B ,C 2C ≥0

U2 = C 2B C 2C subject to: C 2B + S2B ≤ E 2B and C 2C ≤ S2B + S1B − E 2B

Then, using the maximized value of U2∗ one can solve the first generation’s problem: max

S1A ,S1B ,C 1A ,C 1B ≥0

U1 = C 1AC 1B U2∗ subject to: C 1A + S1A ≤ E 1A and C 1B + S1B ≤ S1A + E 1B

The endowments in experiment 3 were chosen in such a way that for the first five years, when there was no deficit spending, the optimal, perfect foresight bequest amount from generation 1 to 2 was S1B∗ = 7. Beginning in year 6, when generation 1 started receiving an endowment (deficit spending) of E 1B = 42 at the start of period B that had to be repaid by generation 2 at the start of period C, so the optimal bequest rose proportionately to S1B∗ = 49. That is, the Ricardian prediction is S1B∗ = E 1B . Cadsby and Frank show that in this experiment as well as several other treatments, the prediction of Ricardian equivalence is approximately correct, and the predictions of a purely myopic model in which no bequests are given, S1B∗ = 0, can be soundly rejected. Figure 1.12 shows individual and average bequests in the treatment we have

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discussed. Following the change in endowment patterns in year 6, bequests jump from an average near 7 to a neighborhood of 49. As Cadsby and Frank acknowledge, however, the introduction of the deficit policy “produced slightly Keynesian results in every case,” that is, the Ricardian equivalence was not perfect. This can be seen in Figure 1.12, where the average bequest lies below 49 even in the final year 10. It may be that such small Keynesian effects account for the continued belief by many in the efficacy of deficit policies. Of course, the real world is also much more complicated than the experimental environment of Cadsby and Frank, so we may wish to view their results as an outer bound on the extent to which the Ricardian doctrine actually holds. Two further experiments build on Cadsby and Frank’s design. Slate and others (1995) change the design so that subjects face uncertainty as to whether the full amount or a smaller fraction of the deficit spending must be repaid. They find that when the probability of full debt repayment is low, Ricardian equivalence fails to hold— generation 1 subjects overconsume and leave too little a bequest. As the probability of full debt repayment becomes larger, so do bequests, which more closely approximate the levels associated with Ricardian equivalence. Ricciuti and Di Laurea (2003) change the overlapping-generations matching protocol so that players are not always in the same role or in fixed pairs. They consider the role of two additional complicating factors that may well prevent members of generation 1 from making neutral bequests: (1) liquidity constraints, and (2) uncertainty about future (second-period) income. They find that both of these complicating factors reduce the likelihood that subjects in the role of generation 1 make bequests that neutralize the debt burden on generation 2, relative to the baseline case. Future work on the economic impact of deficit spending might consider environments where government bonds pays interest, and there also exist markets for private savings. In that case, the more mainstream, neoclassical view, that deficits crowd out private sector investment, could be explored as a rival to the Ricardian view that they have neutral effects.

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5.2 Commitment versus Discretion Another important macroeconomic policy issue concerns the suboptimality of timeconsistent, “discretionary” policies that do not commit the policymaker to a predetermined policy response but are instead optimal for the current situation only, taking current expectations as given and ignoring private-sector expectations with regard to future policies. As Kydland and Prescott (1977) first showed in the context of a twoperiod, expected-inflation-output (Phillips curve) model, following this time-consistent policy can result in the policymaker ratifying the inflation expectations of the public, resulting in an excessive level of inflation and no change in unemployment relative to the social optimum, which involves a zero inflation rate. The social optimum could be implemented by a policymaker who was able to precommit once and for all to zero inflation, but such a “commitment technology” is not typically observed in nature. Kydland and Prescott thus argued in favor of policy rules rather than discretionary policies. Barro and Gordon (1983) recast the inflation-unemployment trade-off as a noncooperative game between the policymaker and the private sector, which is fully aware of the policymaker’s objective function and forms expectations rationally. In an infinitely repeated version of this game, they show that if the policy maker and private sector care enough about the future (have high discount factors), the socially optimal policy (zero inflation, unemployment at the natural rate) may be sustainable as an equilibrium through the use of a grim trigger strategy (many other equilibria are possible as well because the Folk theorem of repeated games applies). The recasting of the policymaker’s problem as a game makes it amenable to testing in the laboratory, and indeed there are two experimental studies that take aim at this issue. Van Huyck, Battalio, and Walters (1995, 2001) use a “peasant-dictator” game to explore policymaking under (1) full precommitment of policy (not observed in nature and thus ripe for experimental testing), (2) discretionary, one-shot policymaking, and (3) the repeated-game case, where reputational concerns from repeated interactions with the private sector may induce the policymaker to embrace policies closer to the social optimum (commitment solution). Subjects in the two-player, two-period stage game are assigned roles as either dictators or peasants. In period 1, peasants are endowed with an amount, W, of beans and must decide how much of these to consume, c 1 ≥ 0, or invest, k ∈ [0, W], earning a gross return of (1 + r )k in period 2; r > 0 is exogenous. The second-period consumption, c 2 ≥ 0, depends on first period investment and the fraction, τ , of the bean harvest taxed by the dictator. Formally, the peasant’s problem is max U = c 1 + c 2 subject to c 1 = W − k and c 2 = (1 − τ e )(1 + r )k

k∈[0,W]

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Here τ e is the expected tax rate; in the commitment case only, there would be no uncertainty about τ as it is announced in advance of peasant’s investment decisions.43 As utility is linear (no need to consumption-smooth), the peasant’s best response correspondence is ⎧ e ⎪ ⎨ W if (1 + r )(1 − τ ) > 1 0 if (1 + r )(1 − τ e ) < 1 k(τ ) = ⎪ ⎩ [0, W] if (1 + r )(1 − τ e ) = 1

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Under commitment, the dictator moves first and solves max R = τ (1 + r )k(τ )

τ ∈[0,1]

The first-order condition can be shown to imply that the social optimum τ ∗ = r/(1 + r ). Given this, it is a weak best response for the peasant to set k = W, and this is the unique subgame perfect equilibrium. Under discretion, the dictator moves after the peasant has made an investment choice and so optimally chooses τ = 1. Knowing this, peasants choose k = 0. A further solution they consider is the Nash bargaining solution, which results in a split-the-surplus tax outcome: τ = τ ∗ /2. Finally, they note that in the infinitely repeated game, implemented with fixed pairings and a constant probability of continuation, if the discount factor is sufficiently high, trigger strategies can support the social optimum commitment solution, as well as other equilibria, such as equal division or the Nash bargaining solution. The experimental design involved three regimes: commitment (C) and discretion (D), implemented as a sequence of one-shot games (random matching) with different timing of moves (dictator/peasant), or (peasant/dictator), and the reputational indefinitely repeated game (R), involving fixed pairings for each supergame and δ = 56 . The other main treatment variable was the peasant’s endowment, W, and the rate of return, r , which were varied subject to the constraint that W(1 + r ) = $1. Mean experimental earnings from at least twenty rounds of the stage game are shown in Figure 1.13 for various cohorts (C), (D), and (R) under various values of W. The shaded regions show feasible repeated-game equilibrium payoffs. Generally speaking, discretionary cohorts (D) are closer to the discretionary equilibrium, commitment cohorts (C) are closer to the commitment equilibrium, and reputational cohorts (R) lie somewhere in between. In summary, they find that reputation is indeed an imperfect substitute for commitment. It is also sensitive to r ; as r decreases, W increases, and reputational concerns are weakened with a corresponding efficiency loss. Arifovic and Sargent (2003) pursue a similar question to that of Van Huyck, Battalio, and Walters (2001): whether the optimal, commitment solution can be implemented by policy makers lacking commitment. The Arifovic-Sargent experiment, however, is in the context of a repeated version of Kydland and Prescott’s expectational Phillips curve model, where the policy maker controls the inflation rate. The motivation for this exercise is also different as it focuses on the predictions of models where the private sector does not have rational expectations (is unaware of the inflation output trade-off) but instead forms its expectations adaptively (the central bank is fully informed of the model). In one model of adaptive expectations due to Phelps (1967), with a sufficiently high discount factor, the government eventually chooses inflation rates consistent with the commitment level. In another model of adaptive expectations due to Sargent (1999) the discretionary “Nash” equilibrium is the only limiting equilibrium. The experimental design involves N + 1 subjects with N = 3–5. N subjects play the role of the private sector, moving first by forming expectations of inflation. Unlike the peasants in the Van Huyck and others experiments, the N private-sector subjects in Arifovic and Sargent’s design know nothing about the inflation unemployment trade-off nor the central bank’s objective but do know the central bank controls inflation. Privatesector subjects have access to the path of past inflation (and unemployment) and can use that information in forming expectations. Thus, the design induces them to form

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expectations of inflation adaptively, consistent with the theory being tested. The mean value of the N inflation expectations each period is regarded as the economy’s expected inflation rate, π e . The lone central banker (CB), picked randomly, moves second. He or she also has access to the past history of unemployment, actual inflation, and, in most treatments, past private-sector expectations of inflation π e . He or she is aware of how the economy works and faces a problem of the form min xt



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t

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(Phillips curve trade-off),

(CB control of inflation)

where Ut is the unemployment rate, U ∗ is the natural rate (set equal to 5 in the experiment) πt is inflation, xt is the central bank’s inflation choice variable (which was constrained only to be nonnegative), and v j t are mean zero, random noise terms, with E v 2j t = σ j2 . The commitment solution has x = π e = 0, while the discretionary equilibrium has x = π e = U ∗ = 5. In the indefinitely repeated experiment, decision

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rounds continued with probability equal to the discount factor δ = 0.98 44 and central bank subjects were paid inversely to the sessionwide average value of the policy loss function, Ut2 + πt2 . The N forecasters were paid based on the average inflation-forecast accuracy. The only treatment variable was the shock variance σ j2 , either large, 0.3, or small 0.03, for both shocks. The main finding is that in nine of twelve sessions, inflation starts out close to the Nash equilibrium level, but over time, the subject in the role of the policy maker steers inflation rather smoothly to within a small neighborhood of the commitment equilibrium for the duration of the experimental session. Further, the private sector’s expectations closely follow the same trajectory and become much more homogeneous with experience. In the other three sessions, inflation fails to converge or remains close to the Ramsey equilibrium value. In four of the sessions where the commitment equilibrium is achieved, there is some “backsliding,” in the sense that inflation temporarily rises to near-discretionary Nash equilibrium levels. Arifovic and Sargent conclude that Phelp’s (1967) model of adaptive expectations appears to best characterize most sessions as it predicts that the central bank exploits adaptive learning by the public to manipulate expectations in the direction of a zero inflation rate. However, they also note that this model predicts much faster convergence than is observed in the data and does not predict instances of backsliding.45 5.3 Monetary Policy On the same subject of monetary policy, Blinder and Morgan (2005, 2008) also consider subjects in the role of central bankers. However, their main focus is on whether monetary policy as formulated by committees (groups of policy makers) outperforms individuals (dictators) in stabilizing the economy and whether there is a difference in the speed of decision making between groups and individuals. The motivation for this research is the observed switch in the 1990s among some developed nations to a more formal committee-based monetary policymaking, as opposed to the prior, informal single-decision-maker policy regime.46 By contrast with the studies discussed in the previous section, the private sector (peasantry) in the Blinder and Morgan studies is eliminated in favor of an automated, stochastic, two-equation coupled system for unemployment Ut (an IS curve) and inflation πt (a Phillips curve) that are used to generate data similar to that of the US economy: Ut − 5 = 0.6(Ut−1 − 5) + 0.3(i t−1 − πt−1 − 5) − G t + e t πt = 0.4πt−1 + 0.3πt−2 + 0.2πt−3 + 0.1πt−4 − 0.5(Ut−1 − 5) + wt

(3) (4)

Here, the natural rate of unemployment is 5, e t and wt are mean-zero random shocks with small known support, and G t represents government fiscal activity, a treatment variable. In this environment, subjects playing the role of the central bank must repeatedly choose the nominal interest in each period t, i t . Notice that monetary policy impacts unemployment with a one-period lag, and via unemployment it impacts inflation with a two-period lag. Subjects were uninformed of the data-generating process, equations (3) and (4), but were told that raising interest rates would lead to lower inflation and higher unemployment and that lowering interest rates would result in the opposite outcome. Subjects were further told that G starts out at 0 and sometime during the first ten periods, would permanently change to either 0.3 or −0.3, resulting in an equal and opposite change in Ut (via (3 )).

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The two-equation system was initialized at the equilibrium for G = 0, all lags of U at 5%, all lags of π at 2%, and i t−1 = 7%. The variables Ut and πt were then drawn according to (3) and (4), and policy makers were instructed to choose i in each of the subsequent 20 periods so as to maximize a known policy objective linear-scoring function, yielding S = 100 − 10|Ut − 5| − 10|πt − 2| points per period. Thus subjects were given the policy targets for U and π , of 5%, and 2%, respectively. Changes made to the nominal interest rate i following the first period cost subjects 10 points per change. A within subjects design was followed: in the first 20 periods, 5 subjects made interestrate choices as individuals (no communication). Then, in the second 20 periods they made interest-rate choices as a group under either a majority or unanimous voting rule. (The reverse order was not considered). Each member of the group received the group score S in points, so there was no difference in payoff opportunities between the two treatments. Blinder and Morgan’s main findings from twenty, five-player sessions are that (1) groups make decisions just as quickly as individuals, (2) groups make better decisions than individuals based on the scoring function, S, and (3) majority or unanimous voting rules in the group treatment yielded the same average scores. These same findings were replicated in a second purely statistical experiment (involving balls drawn from two urns) that was completely devoid of any monetary-policy context. The main finding, that groups outperform individuals, may rationalize the growing trend toward formal monetary policy committees. Three other experimental studies examining monetary-policy decision making by individuals or groups have been conducted by Lombardelli, Proudman, and Talbot (2005), Blinder and Morgan (2008), and Engle-Warnick and Turdaliev (2010). Lombardelli and others adopt a context-laden experimental design that is similar to Blinder and Morgan (2005), though their exogenous, two-equation, data-generating process for inflation and unemployment has fewer parameters and is calibrated to fit UK timeseries data. They divide their sessions into more than two phases, beginning with a pre-experiment survey of prior beliefs. The experiment begins with several periods of individual decision making (choice of interest rates), followed by several periods of group decision making with or without communication (in the latter case, the median interest rate chosen by group members is implemented), followed by several periods of individual decision making and, finally, a repeat of the initial survey instrument. Subjects were given about the same amount of instruction about the economy as in Blinder and Morgan but were asked challenging survey questions such as, “After how many quarters is the maximum impact of monetary policy on inflation felt?” Answers to such questions in the pre-experiment survey were (unsurprisingly) rather poor, but performance on most questions in the postexperiment survey showed some significant improvement. Consistent with Blinder and Morgan’s findings, Lombardelli and others also find that groups outperform individuals using the same kind of linear loss-function score. Interestingly, they report that the group learning experience is not sustained– when individuals return at the end of the experiment to making decisions individually; their scores significantly worsen—see Figure 1.14—even comparing the median of individual scores to the score of groups. This provides even more powerful evidence on the efficacy of group over individual decisions regarding monetary policy. Blinder and Morgan (2008) use their earlier experimental design to study two additional issues related to monetary-policy decision making: the role of group size and of leadership. They report results on four treatments: (1)–(2) four-person groups with or without leaders and (3)–(4) eight-person groups with or without leaders.

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Figure 1.14: Mean/median scores for players over the various phases of the monetary policymaking experiment of Lombardelli, Proudman, and Talbot (2005): individual decision making, group (committee) decision making, and, finally, individual decision making.

In treatments with a leader, the chosen leader was the subject with the highest score in part 1 (individual decision making). However, the leader was endowed with rather weak leadership powers: the ability to communicate the group’s decision, to cast a tie-breaking vote, and to earn a payoff double that of other group members. While Blinder and Morgan are able to replicate their earlier finding that groups outperform individuals, they find that neither group size nor leadership has any statistically significant effect. An implication of these findings is that, while monetarypolicy decision-making committees are a good idea, details of the composition of these committees—the size or designating a leader—are of second-order importance. Future work on this topic might consider actual policy makers as subjects. In all three of the prior studies of monetary policy decision making, the focus is on whether subjects’ interest-rate choices enabled them to achieve target levels for inflation and unemployment given the stochastic data-generating process for the economy. Engle-Warnick and Turdaliev (2010) ask whether the interest-rate choices of subjects playing the role of central bankers can be characterized by an instrument rule— specifically, the Taylor rule (Taylor 1993)—which is optimal for the environment in which they place their subjects. The environment implemented is a purely backwardlooking version of the New Keynesian model due to Svensson (1997). As in the prior studies of central bank decision making, the data-generating processes for inflation, πt , and output, yt , are exogenous and stochastic but are affected directly (in the case of output) or indirectly (in the case of inflation) by the nominal interest rate, i t , chosen each period by the central bank. Subjects were not told the data-generating processes for inflation or output, nor were the labels inflation or output used; instead reference was made to variables A and B. Subjects’ payoff function induced an objective related to the problem of minimizing the expected loss function: Et

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where π is a target inflation rate, set to 5%. Discounting was not implemented; subjects were paid on the basis of their performance in a fifty-round game. In one environment they study, the optimal policy rule (based on the quadratic objective and the linear laws of motion for inflation and output) is the Taylor rule: i t = γ0 + γ1 πt + γ2 yt while in a second model environment, subjects should additionally place some weight on πt−1 . Here the γ s represent coefficient weights for which there are precise (optimal) predictions. The optimal policy predictions involved varying the interest rate between 3.0 and 6.5. More generally, the Taylor principle, that stabilizing monetary policy requires a more-than-proportionate response of interest rates to changes in inflation, requires subjects to set γ1 > 1. Among the main findings, Engle-Warnick and Turdaliev report that while most subjects did not precisely follow the predictions of the optimal Taylor rule, they did manage to keep inflation largely in check, in a neighborhood of the 5% target, and payoffs were not much lower relative to the optimal expected payoff. Further, a clear majority of subjects placed weight greater than 1 on inflation, in accordance with the Taylor principle, though this weight was typically less than the optimal level. Overall, the findings suggest that Taylor’s rule and principle for monetary policy may occur rather naturally to subjects with no prior experience as central bankers, but who face a data generating process for which the Taylor rule is an optimal policy prescription. Monetary policy rules are more often studied in forward-looking versions of the sticky-price, New Keynesian model (as developed, e.g., in Woodford (2003)). Reducedform versions of such forward-looking models typically consist of three equations (leaving out error terms): πt = β E t πt+1 + κ yt

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The first equation for inflation, πt , is the New Keynesian Phillips curve, with β equal to the period discount factor and κ, a parameter capturing the stickiness of prices. The second equation for the output gap, yt , is the expectational IS curve, with ψ representing the intertemporal elasticity of substitution. The model is closed by specification of the central bank’s policy rule—the third equation for the nominal interest rate, i t — and by the assumption of rational expectations. As the equations make clear, time t expectations of future inflation, E t πt+1 , and of the future output gap, E t yt+1 , play a crucial role in in the determination of realizations of time t inflation and output and so the central bank is rightly concerned with how best to manage those expectations in its choice of an interest-rate (policy) rule. Both Pfajfar and Zakelj (2015) and Assenza and others (2013) use learning to forecast experiments to study the stabilizing role of various policy rules in this forward-looking version of the New Keynesian model. Pfajfar and Zakelj (2015) reduce the dimensionality of the expectations problem by replacing E t yt+1 with yt in the expectational IS equation (6) and they fix parameters for β, κ, and ψ. They consider two kinds of inflation-targeting policy rules of the form i t = γ (π˜ t − π¯ ) + π¯

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where π¯ is the central bank’s target level for inflation and π˜ t is either actual time t inflation, πt , or time t expectations of future inflation, E t πt+1 . Their experiment also varies the value of γ from 1.35 on up to 4, so that in all instances the Taylor principle is satisfied. Under rational expectations this further implies that the equilibrium is determinate (locally unique) and stable under correctly specified adaptive learning dynamics (though they also explore determinacy and expectational stability under miss-specified forecast rules). Subjects in this experiment are tasked with forecasting inflation alone, knowing only qualitative features of the underlying model and seeing historical time series on inflation, the output gap, and interest rates. E t πt+1 is taken to be the average of the nine subjects’ forecasts; subjects are paid on the basis of forecast accuracy alone). Pfajfar and Zakelj report that if the policy conditions on expectations of future inflation, E t πt+1 , then the standard deviation of inflation expectations decreases markedly as the coefficient γ is raised from 1.35 to 4, that is, as the central bank becomes more active in responding to deviations of inflation from its target level. They further report that a policy rule that conditions on actual inflation, πt , rather than expectations of future inflation, E t πt+1 , results in the best performance in terms of inflation variability and dampened cyclical tendencies. Intuitively, this policy reduces the weight that expectations of future inflation play in determining current inflation, thus reducing the destabilizing effects of nonrational expectation forecasts. Assenza and others (2013) conduct an experimental study similar to that of Pfajfar and Zakelj (2015), but with some important differences. In one of their treatments they elicit forecasts of both future inflation and the future output gap in accordance with the model. They also consider the case where the γ coefficient on the policy rule is set equal to 1, in which case the Taylor principle does not hold (and so policy does not play a stabilizing role), and they compare this with the case where γ = 1.5 (as in Pfajfar and Zakelj), where the Taylor principle does hold. Their results, as illustrated in Figure 1.15, are striking. The figure shows the evolution of the time series for inflation and the output gap, which have fundamental, steady-state solutions of 2 and 0, respectively, as indicated by the dotted lines. The top panel shows results from two independent groups of subjects who had to forecast both inflation and the output gap under a policy regime where γ = 1, while the bottom panel shows results from two independent groups of subjects in the same treatment but where γ = 1.5. While the output gap appears to converge to 0 in all four sessions, the inflation rate converges to the steady-state value π¯ = 2 only in the treatment where γ = 1.5; when γ = 1, there is evidence of convergence to a restricted perceptions equilibrium (as discussed earlier in the context of the study by Adam (2007)) an inflation level permanently higher than the target level. This is compelling evidence in support of the Taylor principle: to be stabilizing, monetary policy should respond with interest-rate changes that are greater than proportional to changes in inflation from target levels. More recently, experiments have been designed to study the impact of monetary policies in more-structural versions of the New Keynesian model, as opposed to the reduced-form model described before. One approach has been to study the mechanism by which monetary policy changes have real effects. The New Keynesian model assumes that there is some friction by which prices do not adjust immediately to a nominal disturbance. Taylor (1980) and Calvo (1983) assume that only a certain fraction of firms are able to adjust prices each period, due, for example, to contractual constraints or menu costs.47 Mankiw and Reis (2002) posit that only a certain fraction of firms update their information on costs each period because such information is costly to

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acquire. Davis and Korenok (2011) explore the consequences of these two different types of pricing frictions for the real effects of monetary policy in a price-setting game involving monopolistically competitive firms. Given exogenous demand for each firm’s differentiated product and a common marginal cost, profit maximization dictates how each firm should adjust their prices in response to changes in the overall price level. In the absence of any rigidities, an increase in the money supply should lead to an immediate jump in the price level and no change in quantities; however, with price or information rigidities, this same adjustment will take more time (and thus allow monetary policy to have real effects). Davis and Korenok implement Calvo-type pricing frictions by allowing only a third of their firms to change their prices each period, and they implement Mankiw-Reis information frictions by allowing only a third of their firms to see market results (average prices and profits) from the immediately preceding period (another third see this information from two periods prior and the remaining third see information from three periods prior). They find that both of these frictions slow down the adjustment of prices in response to a nominal (money supply) shock that occurs midway through each session. However, the adjustment is much slower than theoretically predicted as subjects exhibit some bounded rationality

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as to how they should change prices when they are able to or when new information becomes available. Indeed, they find that in a control treatment without any pricing or information frictions, adjustment in response to the nominal shock is already quite slow and only slightly faster than the adjustment observed under the two frictions. These findings suggest that bounded rationality in price setting could be an important third factor in rationalizing the real, short-run effects of monetary policy. Similarly, Orland and Roos (2013) study whether human subjects can optimally set prices given free (or costly information) on future desired prices and with variations in the frequency with which price setters are allowed to reset prices (i.e., the Calvo (1983) price-setting probability). They report that the Calvo optimal pricing formula, which serves as a microfoundation of the New Keynesian Phillips curve (5) is a good, though imperfect, approximation to the human subjects’ price-setting behavior; as in Davis and Korenok’s study, subjects are boundedly rational in that they attach too much weight to near-term profits when information on future desired prices is free, and when it is costly, they rely on past prices, a finding that can rationalize hybrid backward- and forward-looking versions of the New Keynesian Phillips curve (e.g., Gali and Gertler 1999). A second approach, as pursued by Noussair Pjafjar, and Zsiros (2013, 2015) and Petersen (2015), has been to implement complete structural versions of a New Keynesian dynamic stochastic general equilibrium model in the laboratory, with different subjects playing the roles of households, firms, and even the central bank—a setup reminiscent of Lian and Plott (1998) and Noussair, Plott, and Riezman (2007). These experimental designs are necessarily simplified approximations of the standard nonlinear model—for instance, both studies have to approximate Dixit-Stiglitz preferences for the variety of goods produced by firms. Noussair and others vary the number of frictions possible from none to monopolistically competitive markup pricing by firms to monopolistically competitive pricing plus menu-cost adjustment and, finally, to include the latter two frictions plus human central bankers setting interest rates with the aim of achieving a target inflation rate. They explore whether demand (inflation) and supply shocks result in more persistent effects on output and inflation in the face of such frictions, and they find evidence for such persistent effects. Petersen further simplifies the New Keynesian model setup, for instance, by getting rid of the competitive labor market and instead eliciting wage and price forecasts to determine the competitive equilibrium wage that is paid to workers. Petersen also automates household or firm sectors to more carefully assess the causal impact of each sector’s decisions on macroeconomic variables. She reports that an automated stimulatory monetary policy that lowers the interest rate on borrowing and saving generally leads to increases in output, but that human subjects acting as households react to the increase in their real wage by underconsuming and oversupplying labor relative to optimal responses. This pioneering work is setting new standards for what can be achieved in the laboratory and for the evaluation of policies in settings closest to the models that macroeconomists actually use.

5.4 Fiscal and Tax Policies Having considered monetary policy, we turn finally to experimental analyses of fiscal and tax policies. Bernasconi, Kirchkamp, and Paruolo (2006) explore how subjects form expectations about fiscal variables, specifically about government expenditure levels and tax revenues. They present subjects with graphical displays showing the historical time path of

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government debt, B, the change in the government debt, B, tax revenues, T , and, in one treatment, the history of government expenditures, G . After viewing the time series, subjects have up to two minutes to form one-step-ahead forecasts of taxes and, in one treatment, government expenditures as well. The novelty of their design is that the data presented to subjects are the actual OECD historical time-series data taken from one of fifteen European states primarily between 1970 and 1998. Subjects were not informed of the country from which the data come. In most treatments they were told the name of each historical series, such as ‘tax revenue’. Subjects were not particularly knowledgeable about relationships between G , T , and B, a fact the experimenters view as a strength of their study, as it parallels the largely ad hoc, time-series-econometric approach that has been taken to understanding the sustainability of fiscal policies. Subjects are rewarded in a somewhat complicated fashion according to their forecast accuracy, which is assessed every two periods. Thus, this is a “learning-to-forecast” type of experiment. However, like the monetary policy experiments discussed in the last section, subjects are being presented with data that have a more realistic macroeconomic flavor, for example, in terms of magnitudes, causal relationships, and the like. Unlike the monetary policy experiments however, there is no feedback from subjects’ choices (expectations) to subsequent data realizations; subjects are truly atomistic in this environment. The main finding is that changes in subjects’ expectations, G E and T E , compare poorly with a time-series, vector autoregression model for G and T , estimated using the same historical data presented to subjects. The model that best fits the change in subjects’ expectations appears to be one that is weighted adaptive, with heaviest weight placed on recent forecast errors. Riedl and van Winden (2001, 2007) design a one- (closed) or two-country (international) experimental economy that is quite similar to the setup of Noussair (1995, 1997) to explore government tax policies in the financing of unemployment benefits. This experimental work is particularly notable for being the first laboratory experiments ever commissioned by a government agency—the Dutch Ministry of Social Affairs and Unemployment—to inform on macroeconomic policymaking. Within each country there are two player types, consumers and producers, two production goods, K (capital) and L (labor), and two final goods, X and Y. In the international economy, the goods K and X are tradeable between nations, while L and Y are not. Producers are endowed with cash and a CES production function that uses both K and L as inputs. Consumers are endowed with preferences for the two goods and leisure and with amounts of K , L , and money. In the international setting, in the “large” country, consumer and producer endowments are seven times those for the other, “small” country; the number of subjects in each country is the same. For each unit of “unsold” labor, L − L , consumers get an unemployment benefit, w 0 , from the exogenous government entity (not a player); this becomes an additional source of money for consumers, in addition to money earned by selling L units of labor at wages w and K units of capital at rents r to producers who require these as inputs to produce X and Y. Consumers also earn money from consumption of these final goods according to their utility functions. Double-auction markets for input goods open first, then production occurs, and then double-auction markets open for final goods. The main focus of these studies is on the unemploymentbenefits policy. Unemployment-benefits in country k are financed (as in many European countries) by a tax rate τ k , applied to units of labor income, w k L k . This tax is paid by producers, who are induced in the design to want to maximize after-tax profits. In the first half (eight periods) of their experimental sessions, τ k is held constant at the general

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equilibrium level associated with a balanced budget. In the second part, the benefit tax is adjusted dynamically up to some limit so as to gradually close any deficits. Specifically, the tax rate is set according to the ratio of paid benefits to the tax base in the prior period, 

k τt+1

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where w0 is the constant benefit level. Riedl and van Winden report that under the stable tax regime of the first half of sessions, wages are too low relative to the marginal revenue product and unemployment is too high, though both measures are moving slowly toward the induced equilibrium levels (as demonstrated in regressions models of the form (1)). This is attributed to producers’ reluctance to employ sufficient labor and capital given uncertainties about prices and revenues earned on output. The result is a deficit in the employment benefits program.48 Following the switchover to the dynamic tax policy, tax rates immediately rise in response to the employment benefits deficit and eventually plateau out, rising from 38% to around 70% and resulting in a more balanced budget. However, this steep tax increase in benefits taxes is associated with a rather large increase in unemployment and reduction in real GDP relative to the constant tax rate policy. It appears that the benefits tax increases on producers discourages them from hiring labor and this, together with an excess supply of labor by consumers, leads to much lower wages and higher unemployment, which leads to further demand for benefits, that is, a “vicious cycle.” Future work on this topic might consider alternative policies for maintenance of a balanced budget, including variations in the amount and duration of the unemployment benefit, w0 . Finally, several experimental studies address redistributive social policies associated with the welfare state.49 Van der Heijden and others (1998) test a possible explanation for the widespread and sustained public support for pay-as-you-go social security systems in which old, retired agents are paid benefits from taxes on the income of the working young. Viewing such systems as a repeated game played between successive generations of young and old agents, they propose that the social norm of transfers from young to old may be sustained as a sequential equilibrium of the infinitely repeated game by a grim trigger strategy: if one young generation ever failed to make transfer payments to the old, subsequent young generations would revert to a perpetual punishment strategy of transferring zero to all future old generations, including the defecting generation. Their argument relies on the ability of generations to monitor transfers made by earlier generations; thus in one treatment, this monitoring ability is present, while in another it is not. The experimental design involves implementation of an overlapping generations environment in which each of eight subjects takes a randomly ordered turn as a young agent making a voluntary transfer to an old agent. Subjects are young in one of the eight periods t, are old in period t + 1, and then no longer participate in the round (dead). Young agents have an endowment of nine units of the consumption good, but only seven of these units are transferable to the current old subject, who has an endowment of one nontransferable unit. Payoffs are proportional to the product of consumption in the two periods of life. The payoff to the subject in the role of generation t is C 1t × C 2t = (9 − Tt )(1 + Tt+1 ), where Tt is the transfer made by generation t. After eight

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transfer decisions, the round is over and a new one begins involving the same subjects, who make transfer decisions in another random order. However, an infinite horizon was not implemented: subjects knew that fifteen eight-round games would be played, and consequently there are end-game effects.50 Still, the results are interesting: while subjects did not achieve the efficient, payoff-maximizing transfer of T = 4 units from young to old, they did transfer on average about 2 units per period, with a slight dropoff over time. Further, the amount of transfers was independent of whether monitoring of past transfers was possible; this finding may be due to the (unnatural) repeated interactions among groups of eight subjects. Indeed, these results are reminiscent of experimental studies showing positive contributions in repeated, linear, voluntary contribution mechanisms (see Ledyard 1995). However, in this case, the transfers are dynamic and intertemporal, the hallmarks of macroeconomic systems. The willingness of subjects to sustain a social norm of (low) transfers from young to old, regardless of the ability to monitor, may nevertheless rationalize support of pay-as-you go systems as arising from hardwired preferences for “fairness.” Offerman, Potters, and Verbon (2001) study a similar multigeneration “pension” game also in an overlapping-generations economy but with an indefinite horizon so that mutual cooperation in terms of contributions to pension benefits is a potential sequential equilibrium supported by a grim trigger strategy. Specifically, they consider the moves made by a sequence of players P1 , P2 , . . . ,Pt ,Pt+1 . . . who face the game shown in Table 1.7. Player P1 makes no choice but gets a payoff of 50 (30) if P2 chooses A (B). The payoff of each player Pt , t > 1, depends on his or her own choice of A or B at time t and the choice of A or B by the following player, Pt+1 , and has payoffs as given in Table 1.7. Subjects were queued up to play the game just once (with no repetition) and may have had the chance to play depending on the realization of the constant 90 continuation probability following the decision of player P2.51 The cooperative equilibrium has all players choosing A. Offerman and others studied two treatments, a baseline treatment where subjects made choices but also recorded their strategies for all possible histories using a strategy method and a recommendations treatment, where the baseline treatment was supplemented with recommendations made by the experimenter on what actions subjects ought to choose, that followed the grim trigger strategy that sustains the cooperative outcome. They report a low and statistically indistinguishable rate of cooperation (choice of A) in both treatments: 13.8% in the baseline and 29.3% in the recommendations treatment. Further, they report that in the baseline treatment, there is not much evidence for trigger strategies in the strategies submitted by subjects— just 15.4%; most subjects are playing unconditional noncooperative strategies (always B). While the use of trigger strategies does climb to 46.1% in the recommendations treatment, this does not suffice to sustain a social norm of cooperation with respect to pension contributions. Offerman and others thus conclude that there is not much

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evidence that cooperation with regard to intergenerational pension transfers is selfenforcing, despite the theoretical possibility of such an outcome. However, we generally do not observe self-enforcing social security systems. Instead, participation is compelled by law. Thus future laboratory work on social security/pension systems might investigate the consequences of government-imposed taxes on labor income for consumption, savings, and capital formation under both payas-you go and fully funded (private accounts) systems. Such studies would have the added benefit of informing current policy debates regarding the merits of these two different systems. Cabrales, Nagel, and Rodriguez-Mora (2012) also study whether an efficient, redistributive social contract can emerge in the laboratory. In their case, the redistribution is not from young to old but from rich to poor, and the extent of the redistribution implemented by the government is decided by voters under various voting procedures. The basic-stage game involves nine players and consists of two rounds. In the first round, subjects choose high or low effort with high effort costing c and low effort being costless. Those who choose high effort earn high income y h with probability 23 and low income y l otherwise. Those choosing low effort earn low income y l with certainty. Once effort choices and incomes are determined and revealed to subjects, the next round of the game is played, in which all subjects vote on whether to equalize (“redistribute” ) incomes so that each player i = 1, 2, . . . , 9 receives 19 i9=1 yi . The actual equalized income level is revealed to subjects in advance of the vote. Three voting procedures are considered: majority rule, unanimous consent, or majority-rule voting only by those who chose high effort. In a fourth treatment, incomes are randomly assigned and subjects vote only in the second round under majority rule. If income equalization fails according to the voting procedure, then each subject gets the income they earned, y l or y h . A one-shot version of the two-round game under majority rule is like a stag hunt game with two Pareto-ranked equilibria: an inefficient “Hobbesian” equilibrium where all choose low effort and vote to equalize incomes and a Pareto superior equilibrium where all choose high effort and vote against equalization. However, in the finitely repeated game, which is the focus of this study, there exists an even better, social insurance equilibrium, which the authors label a Rousseau-type “social contract.” In this sequential equilibrium, everyone chooses high effort but votes for equalization— that is, they recognize that some ( 13 on average) choosing high effort earn low income due simply to bad luck. This equilibrium is sustainable until a certain number of periods from the finite end (when there is a switchover to the outcome where all supply high effort but vote against equalization) via the threat to revert to the “Hobbesian” equilibrium of low effort and redistribution. The main finding from several sessions involving fifty repetitions of the tworound, majority-rule game is that the social contract equilibrium is not observed. With experience, most groups of subjects move closer to or achieve the inefficient Hobbesian equilibrium. When a majority of subjects are poor (which occurs 75% of the time), redistribution got a majority of votes 90% of the time, while when a majority of subjects were rich, redistribution succeeded only 15% of the time. Similar results are observed in the other three treatments—unanimous voting, voting restricted to those choosing high effort, and random exogenous effort with majority voting. These results suggest that social insurance contracts are unlikely to emerge on their own. However, the fact that redistributive welfare policies are observed in nature suggests that some critical element is missing from this experimental design. Some possibilities to consider are (1) whether longer-term, binding redistributive policies—in effect for multiple periods—might aid

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in the formation of social insurance policies or (2) whether political institutions, such as a presidential or parliamentary representation system might play some role in the implementation and sustenance of social insurance policies.

6 CONCLUSIONS Certainly the most important development in macroeconomics over the past several decades has been the widespread adoption of fully rational, microfounded, calibrated, dynamic stochastic general equilibrium models as laboratories for evaluation of macroeconomic theories and policies. In this chapter I have summarized the small but growing research on an alternative methodology, which can be characterized as the use of experimental laboratories as laboratories for evaluation of macroeconomic theories and policies. As we have seen, (contrary to the claim of Sims (1996)) “crucial data” in support of macroeconomic models and theories—especially, (though not exclusively) those that are microfounded—can be gathered in the experimental laboratory. Such experimental tests can complement empirical analyses using field data, as in analysis of intertemporal consumption/savings decisions, rational expectations, efficiency wages, or Ricardian equivalence. On the other hand, there are many macroeconomic theories, for instance, on the origins of money, sunspots, speculative attacks, and bank runs, for which the data critical to an assessment of the theory are not available in the field. In the laboratory we can manufacture such data to meet the precise specifications of the theory being tested. In macroeconomic systems such data include not only individual choices over time, but also frequently involve individual expectations of future variables—data which are not readily available in the field. Indeed, one innovation of macroeconomic experiments is the division of experimental designs into two basic types. In “learning-to-optimize” designs, one observes whether individuals can learn over time to maximize some well-defined objective function as in most microeconomic laboratory experiments. However, many macroeconomic experiments make use of a less conventional “learning-to-forecast” design in which subjects’ expectations of future variables are elicited; given these expectations, their optimization problem is solved for them by the experimenter (computer program) and they are then rewarded solely on the basis of expectations accuracy. Macroeconomic experiments have yielded other innovations, including the implementation of overlapping generations and search-theoretic environments in the laboratory, the use of indefinite repetition to implement discounting and the stationarity associated with infinite horizons and a methodology for assessing whether laboratory time-series data are converging toward predicted equilibrium levels (as in equation (1)). Much further experimental research on macroeconomic topics remains to be done. Throughout this survey I have suggested a number of extensions to existing experimental studies that I believe would be useful experiments. However, there are a number of macroeconomic topic areas for which there are little or no existing experimental studies, and these areas are real targets of opportunity.52 In this category I would place analysis of (1) sticky price mechanisms such as staggered wage and price setting, (2) habit formation, relative concerns, and the durability of expenditures in intertemporal consumption decisions, (3) the search and matching approach to understanding unemployment, job creation, and destruction (as developed by Mortensen and Pissarides (1994)), (4) Tobin’s q-theory of investment determination and the observed lumpiness

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in aggregate investment dynamics, (5) various theories of the term structure of interest rates, (6) the irrelevance of financial structure (stock or bond financing) as in the Modigliani-Miller theorem, (7) the role of credit market imperfections in business cycle fluctuations, (8) policies that have been proposed to stabilize balance-of-payments crises in developing countries, (9) some of the explanations for cross-country differences in economic growth, including legal-institutions and human-capital accumulation, and (10) the existence of political business cycles. The field of macroeconomics is among the final frontiers in the continuing transformation of economics into an experimental science. As this survey illustrates, that frontier is beginning to be populated, but only time will tell whether mainstream macroeconomists join their microeconomic brethren in accepting the relevance of laboratory methods. If past history is any guide, for example, the rational expectations/microfoundations revolution of the 1970s and 1980s, another revolution in macroeconomic methodology may well be at hand.

ACKNOWLEDGMENTS For helpful comments and suggestions on earlier drafts, I thank Antoni BoschDoménech, Gabriele Camera, Frank Heinemann, John Kagel, Rosemarie Nagel, Soiliou Namoro, Charles Noussair, Andreas Ortmann, Daniela Puzzello, Alvin E. Roth, JeanRobert Tyran, Frans van Winden, Randall Wright, Daniel J. Zizzo and Students of the Barcelona LeeX Experimental Economics Summer School in Macroeconomics.

NOTES 1. Indeed, the term macroeconomic experiment does not even typically refer to laboratory experiments involving human subjects but rather to computational experiments using calibrated dynamic stochastic general equilibrium models as pioneered in the work of Finn Kydland and Edward Prescott (1982). Even these experimental exercises have been ruled out as unacceptable by some. Sims (1996, 113) writes: “What Kydland and Prescott call computational experiments are computations not experiments. In economics, unlike experimental sciences, we cannot create observations designed to resolve our uncertainties about theories; no amount of computation can resolve that.” 2. Of course, this assumption is generally false. As Fisher (1987) points out in his New Palgrave entry on aggregation problems, “the analytic use of such aggregates as ‘capital’, ‘output’, ‘labour’ or ‘investment’ as though the production side of the economy can be treated as a single firm is without sound foundation.” Fisher adds that “this has not discouraged macroeconomists from continuing to work in such terms.” Indeed, one may think of macroeconomics as an impure language with bad grammar and borrowed words but a language nonetheless, and one with many users. 3. The current state of macroeconomic experiments mirrors that of political science experiments. As Morton and Williams (2010, 16) write: “Despite the remarkable growth [in experimental political science] the view that. . . experimental methods have less use in political science as compared to other sciences, is still prevalent. The modal political scientist has not conducted an experiment and experimental work is still seen as not that relevant to some weighty political science questions of interest.” 4. See, again, Sims (1996, 107), who writes: “Economists can do very little experimentation to produce crucial data. This is particularly true of macroeconomics.” 5. Indeed, if one were to take the typical “representative agent” macroeconomic model quite literally, then all that is really needed is a single agent (albeit a far-sighted rational one), and it is certainly feasible to conduct individual-decision experiments in the laboratory. 6. This follows the random termination procedure used to implement infinitely repeated games as pioneered by Roth and Murnighan (1978). 7. Carbone (2006) explores this heterogeneity in consumption/savings behavior econometrically. 8. See Kirman (1992) for a discussion of the limitations of the representative agent assumption.

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Chapter 1 9. This regression model was first proposed to study the convergence of experimental panel data in Noussair, Plott, and Riezman (1995). 10. Lei and Noussair (2002) also consider a planning-agency treatment in which the social planner is replaced with a group of five subjects (as in the market treatment), who together attempt to solve the social planner’s problem. Convergence results for this planning-agency treatment are somewhat better than in the social-planner treatment but still worse than in the market treatment, based on regression findings using the model (1) t−2 i 11. Starting in period 1 with y j,1 and iterating on (2), we can write E [y j,t ] = λt−1 i =0 λ μ j + j y j,1 + t−2 i i =0 λ j  j,t−i . Given λ < 1, and for t sufficiently large, we have E [y j ] = μ j /(1 − λ j ). 12. The issue of whether the length of time taken up by a decision round matters is an unexplored issue. This issue is tied up with aggregation of decisions. Macroeconomic data are typically recorded at low frequencies, for example, monthly or quarterly “consumption,” whereas in laboratory studies, the length of time between decisions is, out of necessity, much more compressed—a few seconds to a few minutes. 13. The neuroeconomics chapter by Camerer et al. (Chapter 3 in this volume) discusses the neural evidence for β − δ preferences. 14. Hommes et al. (2005) use a similar approach to study expectation formation in a simple asset-pricing model. 15. Specifically, denote the ratio of marginal supply to marginal demand at the equilibrium price by σ (λ) = S  ( pt∗ )/D  ( pt∗ ). Stability under naive expectations requires that −1 < σ (λ) < 1. Otherwise, there is instability, and this can be determined by varying λ. 16. Other studies exploring the impact of monetary policy on expectation formation in the New Keynesian model are addressed later in Section 5.3. 17. Noncorner (interior) rational expectations solutions are possible via a simple change to the payoff objective, for example, guess the number closest in absolute value to 100 − p x¯ . 18. The p = 1 case corresponds to a pure coordination game; see Ochs (1995) for the relevant experimental literature on such games. 19. Nagel (1995) also considers the case of p = 23 and p = 43 , and repeated versions of all three games. 20. That material, while highly relevant to the literature on experimental macroeconomics, will not be repeated here; – the interested reader is referred to Ochs (1995). See also Camerer (2003, chapter 7) and Devetag and Ortmann (2007). 21. One difference is that Capra et al. use a “call market” clearing mechanism for the capital market, as opposed to the double-auction mechanism used by Lei and Noussair (2007). The difference between these two mechanisms is discussed in Section 3.3. 22. Specifically, for each session they estimate the equation Y j t = α/t + β t−1 t +  j + v j,t , where j indexes each indefinite sequence, or “horizon,” within a session. The dependent variable Y j,t is either aggregate 5  welfare, U (c t ) = i =1 ui (c ti ), or the aggregate capital stock, kti = i5=1 kti . The two asymptotic estimates for each session—the estimates of β for each of the two dependent variables—are the squares shown in Figure 1.4. 23. The possible returns from the five banks are known to belong to the set: {( 13 )r ∗ , ( 23 )r ∗ , r ∗ , ( 43 )r ∗ , ( 53 )r ∗ }. 24. The latter finding may seem at odds with Garratt and Keister’s findings, but note that Schotter and Yorulmazer don’t have forced shocks, so their setup is closest to Garratt and Keister’s setting without forced shocks, in which panics were rarely observed. 25. John Maynard Keynes talked about “animal spirits” as a source of investment volatility. Charles McKay talked about the “madness of crowds” in documenting famous financial fiascos. These are references to the role played by nonfundamental, extrinsic variables, or “sunspots”, in economic activity. The term sunspot derives from the work of William Stanley Jevons, a nineteenth-century economist and polymath who championed the notion that the solar cycle was responsible for variations in crop yields and, therefore, business cycles. Today we honor Jevons’ folly by referring to nonfundamental variables that are extrinsic to economic activity as “sunspot variables.” 26. Notice from Figure 1.4 that two out of five buyers/sellers prefer the high equilibrium and two out of five prefer the low equilibrium and the remaining buyer and seller are indifferent. Thus, the equilibria are not Pareto rankable. 27. In Carlsson and van Damme’s approach, players facing a game of complete information with multiple equilibria behave as though it were a perturbed global game of incomplete information where the payoffs are determined by a random draw from a given class of games and players have a noisy signal of the chosen game. 28. There is some debate about whether bank runs and financial crises are caused by fundamental or nonfundamental (sunspots).

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29. Surprisingly, Bernasconi and Kirchkamp do not consider the same parameterization of the OG money model as examined by Marimon and Sunder (1993, 1994, 1995), so a direct comparison is not possible. 30. Experiments on learning in games similarly show that subjects’ beliefs and action choices do not necessarily coincide, and that convergence may or may not obtain as subjects acquire experience. See, for example; Ehrblatt et al. (2012). 31. A consol is a bond with no terminal date paying a certain dividend per period forever. 32. In the theory, there is a continuum of agents divided up equally among the three types. In the laboratory, we must work with finite numbers, and one consequence is that stationary Nash equlibria under the continuum-of-agents assumption may no longer exist (as individual agents may exert some market power). In practice, with sufficiently many agents—Duffy and Ochs (1999, 2002) used populations of size eighteen to thirty subjects—one can minimize such strategic considerations so that the Nash equilibria of the theory are approximate Nash equilibria of the associated “game” played by the finite populations of subjects available to laboratory researchers. See the appendix of Duffy and Ochs (2002) for some evidence in support of this proposition. 33. In all such models there always exists a no-trade equilibrium as well, so experimental testing also addresses this equilibrium-selection question. 34. Interestingly, this same lack of speculation finding is also obtained in an agent-based model simulation conducted by Marimon et al. (1990), which was the inspiration for both the Brown and Duffy and Ochs studies. 35. See also Duffy and Ochs (2009) and Duffy, Xi, and Lee (2013), who study the role of information on the prior play of opponents that they liken to credit histories provided by third-party credit bureaus. 36. As Akerlof and Shiller (2009, 43) observe, an earlier generation of macroeconomists, including Irving Fisher and John Maynard Keynes, thought that money illusion played an important role in macroeconomic phenomena, but among modern macroeconomists, “it has become taboo to believe in money illusion.” 37. For one early attempt, see the following discussion of Arifovic (1996). 38. Most estimates based on microeconomic data find the compensated elasticity to be small or even negative. 39. The first experiment involving both input and output markets was conducted by Goodfellow and Plott (1990). 40. As in Arifovic (1996), one can think of all the subjects in Fisher (2001) as residing in the domestic country only but having access to foreign currency. 41. For instance, random walk models have consistently outperformed any economic theory of exchange-rate dynamics. 42. More precisely, Okun’s law predicts that a 1% increase in unemployment above the natural rate is associated with a reduction in real GDP of 2% to 3%. Lian and Plott find evidence for a negative and roughly proportional trade-off between changes in unemployment and real GNP. 43. One advantage of laboratory research is that commitment regimes can be credibly implemented by the experimenter! 44. A upper bound of 100 rounds was imposed, and sessions were conducted for two hours. 45. One version of Sargent’s (1999) adaptive learning dynamics, constant-gain learning, predicts long endogenous cycles (“escape dynamics” ) which can rationalize instances of backsliding from the commitment equilibrium to the discretionary equilibrium and back. 46. For instance, in 1997, the Monetary Policy Committee of the Bank of England replaced the Chancellor of the Exchequer as the primary decision maker on short-term interest rates. 47. Wilson (1998) designs an experiment to explore Mankiw’s (1985) menu-cost explanation for sticky price adjustment in a setting where subjects play the role of monopoly firms and must decide whether to adjust prices in response to shocks to aggregate demand. 48. Budget balance requires that τ k w k L k = w 0 L − L kt . 49. For a more general survey of experimental work on redistributive preferences, see Tausch, Potters, and Riedl (2013). 50. Under these conditions, the repeated game-equilibrium-sustaining transfer does not exist as it would unravel via backward induction. 51. Offerman et al. drew a random sequence of numbers to determine the length of the indefinite horizon in advance. Indefinite sequences ranged from four to twelve rounds, but they always recruited at least ninteen subjects to participate in a given session. While they did not tell subjects the length of the supergame, it could be inferred from the finite number of subjects in the room that there was an upper bound to the number of rounds that could be played. 52. If I had any sense, I would keep this list of topics under my own hat, though most seem (to me) to be fairly obvious candidates for experimental analysis.

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2 Using Experimental Methods to Understand Why and How We Give to Charity Lise Vesterlund

1 INTRODUCTION Individuals who are concerned for a nonprofit’s mission benefit from activities that increase the nonprofit’s output. As these benefits are enjoyed by anyone with similar concerns, donations are both nonrival and nonexclusive, and they can be modeled as voluntary contributions to public goods. Noting the inherent free-rider problem, much theoretical and applied research has been done to understand how voluntary provision of public goods nonetheless is secured and how it can be improved. The objective of this chapter is to review the literature that uses experimental methods to shed light on voluntary giving. The chapter builds on Ledyard’s highly influential review of public good experiments in the first volume of the handbook (Kagel and Roth 1995, Chapter 2). Recognizing the substantial work on the topic, Ledyard limited his review to the linear public good game commonly examined in the laboratory, and he emphasized research on factors that trigger cooperation in that environment. The literature on voluntary giving has grown substantially since the first volume. Much work has been done to further determine the factors that drive cooperation, and many new questions have emerged. The essential role of heterogeneity in beliefs and preferences has come to light, and spurred by Nobel Prize Winner Elinor Ostrom, there has been a growing interest in the mechanisms groups use to ensure that public goods are provided. Studies examining the effect on giving of endogenous group formation, and of punishments and rewards more generally, have been significant.1 Another strand of the literature has focused directly on voluntary contributions to charities and nonprofits. This literature investigates both the motives for giving and the mechanisms nonprofits use to raise funds. In contrast to the literature on group-selected mechanisms, the assumption is that the contribution mechanism is selected by those soliciting funds. Just as it was not possible for Ledyard to cover the entire literature on public good experiments, it is not possible for this review to do justice to the large body of research

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that has been conducted since the first handbook.2 With the literature on cooperation in the linear public good game being relatively well surveyed, I focus instead on research examining contributions to nonprofits.3 I first discuss the literature on motives for giving. In doing so it becomes clear that researchers have expanded the set of giving motives considered and the environments used to identify these. The objective is no longer to determine whether individuals are selfish or cooperative but rather whether giving can be viewed as rational and, if so, what set of preferences are consistent with the observed pattern of giving. To address these questions researchers have moved beyond the linear public good environments and have developed innovative designs that better delineate between the alternative models of giving. In building on the charitable giving literature the review centers on studies that examine between the extent to which donations are motivated by a concern for others or by a concern for self. Following the review on motives for giving, I proceed to the literature on fundraising mechanisms. While the literature on mechanism design shows that optimal provision of public goods in some cases can be achieved through the correct use of taxes and penalties, it is unlikely that a fundraiser will or can select a donation mechanism that secures comparable outcomes. Fundraisers differ from the classic social planner, both in their objective and in the tools that are available to them. Rather than maximizing aggregate welfare, the fundraiser’s objective is assumed to be one of contribution maximization, and the tools under consideration are limited to those that secure voluntary participation by donors.4 Research in this area aims to determine whether and why the mechanisms fundraisers employ are successful in raising contributions. For example, I report on studies that investigate why fundraisers announce past contributions, why they tend to rely on lotteries rather than the theoretically superior all-pay auction, and why they tend to match rather than rebate contributions. The two strands of the literature reviewed—motives for giving and mechanisms used to solicit gifts—can be seen as representing, respectively, the supply and demand side of the market for voluntary contributions. Experimental investigations of either side reveal results reflective of the interaction between the two. As the aim increasingly is to understand behavior in the market for charitable donations, researchers have begun to examine environments that better capture the market of interest, be it more-sophisticated laboratory studies or the field itself. Much research is now done by examining field environments with public good characteristics. A consequence of this field-oriented shift, both in the questions and environments that are being examined, is that experimental studies on public goods increasingly are helping to form the debate on charitable giving.

2 PREFERENCES FOR GIVING Practically every paper on charitable giving begins by noting that the nonprofit sector constitutes a significant portion of the US economy. According to the Philanthropy Panel Study (PPS), 65.4% of all households contributed an average of $2,321 to nonprofits in 2008. While more than half of these donations are directed to or through the individual’s house of worship, it is still the case that substantial contributions are made to complete strangers or organizations that cannot reciprocate the generosity. Much of the literature focuses on understanding what motivates this latter type of unconditional transfer. That is, the emphasis is on explaining why people give their

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money to activities that, while benefitting others, provide no transparent material benefit to the individuals themselves. Information on donor’s beliefs on the contributions by others is needed to infer an individual’s motive for giving. It is, therefore, difficult to determine motives from data on actual donations, be it from surveys, tax returns, or organizational-level data. An advantage of laboratory experiments and experimental techniques in general is that they permit the manipulation of information needed to infer motives. This section will discuss the many designs researchers have used to determine why people give. Prior to reviewing the literature, it is beneficial to remind ourselves how donations to public goods are modeled and, in particular, how this framework relates to the experimental designs commonly used to study giving in the laboratory. In the standard model of voluntary giving, individuals, i = 1, . . . , n, are assumed to care about private consumption xi and the total provision of a public good, G . Individual i ’s contribution to the public good  is denoted by g i and the provision of the public good is the sum of these, that is, G = in=1 g i . With consumption of the public good being nonrival and nonexclusive, everyone benefits from the total provision of the public good. Denoting i ’s income by wi and normalizing prices such that pG = p x = 1, i ’s budget constraint is given by g i + xi ≤ wi . Representing preferences by a continuous and strictly quasiconcave function Ui (xi , G ), i ’s preferred provision level is given by the continuous demand function G ∗ = qi (wi + G −i )

(1)

 where G −i = j =i g j is the amount given by others to the public good. The demand function qi (.) is simply the individual’s Engel curve for the public good. As shown Blume, and Varian (1986), there exists a unique equilibrium   ∗ ∗ by Bergstrom, g 1 , g 2 , . . . , g n∗ of this game when both the public and the private good are normal goods, where i  s gift is given by g i∗ = max {0, −G −i + qi (wi + G −i )}

(2)

Since a donor does not consider the effect his or her contribution has on similarly motivated individuals, the standard free-rider problem arises and equilibrium contributions are inefficiently low. This is easily seen in the two-person example shown in Figure 2.1. Contributions by individuals 1 and 2 are measured on the horizontal and vertical axis, respectively, and the intersection of the two downward sloping bestresponse functions, BRF1 and BRF2 , demonstrates the resulting Nash equilibrium (g 1∗ , g 2∗ ). Looking at an individual’s indifference curves through (g 1∗ , g 2∗ ) and recalling that utility is strictly increasing in giving by others, it is apparent that there exist contributions that are preferred by both contributors and result in greater overall provision of the public good. That is, the equilibrium provision of the public good (G ∗ = g 1∗ + g 2∗ ) is inefficiently low. This voluntary public good model is used for modeling contributions to nonprofits and to charities. When a person donates to a charity, the motive for giving is thought to be a concern for the well-being of those who receive services from the charity, be it children securing an education, the hungry getting food, the homeless receiving shelter, and so on. The motive for giving is one of altruism, with the return from giving arising from the effect donations have on the well-being of the recipients.5 As the benefit results

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g2 U1

BRF1

U2

g2* NE BRF2 g1

g1* Figure 2.1: Voluntary contribution equilibrium.

from the impact of the gift, rather than the gift itself, an individual’s donation will benefit the recipient and the donor, as well as anyone else who is concerned for the recipient’s well-being. Thus, the recipient’s well-being is a public good in an altruistically inclined population (Becker 1974). Equivalently when donating to a broader set of nonprofits, an altruist is someone who cares about the output that results from the donation. In studying giving in the laboratory, most research centers on examining behavior in the dictator game and in the linear public good game. In the dictator game a decision maker is given an endowment and asked how much of the endowment he or she would like to give to an anonymous recipient. In the classic setup the recipient is another participant in the experiment (e.g., Forsythe et al. 1994); later studies look at transfers to recipients outside the laboratory (e.g., Fong and Luttmer 2011) or let an existing nonprofit replace the role of the recipient (e.g., Eckel and Grossman 2006). In capturing the response to a request to give to others, the dictator game has been used to characterize preferences for giving.6 However with only one decision maker, the dictator game does not capture how the incentive to free ride affects the interaction between potential donors. The linear public good game (frequently referred to as the voluntary contribution mechanism, or VCM) by Isaac, Walker, and Thomas (1984) provides a strategic environment where it is possible to study the interaction between multiple donors. Participants in the VCM are paired in groups of n people, and each is given an endowment wi , which they must distribute between a private and a public account. Payoffs are linear, with the private account generating an individual return of r and the public account generating a return of m to every member of the group. Thus an allocation to the public account, g i , constitutes a contribution to a public good. The individual return from giving, m/r , is referred to as the marginal per capita return (MPCR), and the individual’s payoff from contributing g i equals πi = r (wi − g i ) + m

n  i =1

gi

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 Thus the individual’s return from the public account is m in=1 g i . Contributing to the public account generates a collective benefit of (n − 1) m to the other group members and costs the individual r − m. To study a social dilemma, it is assumed that 1 < mr < 1, such that it is socially optimal to give, yet costly for the individual to do so. n Compared to the public good game demonstrated in Figure 2.1, the payoffs of the linear VCM induce preferences where deviations from equilibrium are welfare improving, placing the dominant strategy and the efficient outcome the boundary  of the strategy  at ∗ ∗ ∗ , g , . . . , g space, the equilibrium prediction being zero provision g 1 2 n = (0, 0, . . . , 0),  and the efficient outcome being full provision g 1∗ , g 2∗ , . . . , g n∗ = (w1 , w2 , . . . , wn ) .7 Common for the dictator and public good game is that individuals who aim to maximize their own earnings are predicted to give nothing. Experimental investigations of both games reveal behavior different from this prediction. In the classic dictator game, individuals contribute on average 25% of their initial endowment to a random participant (see, e.g., Forsythe et al. 1994). In the VCM, contributions typically start off around 50% of endowments and then decrease with repetition, but they remain substantial even when participants have had time to gain experience in the game (see, e.g., Isaac and Walker 1988; Ledyard 1995; Holt and Laury 2008; Croson 2007, 2008 for reviews). Researchers have used both the dictator and the public good game to examine what motivates charitable giving. Contributions in both environments can be seen as evidence that individuals are concerned for the welfare of others. Thus by manipulating the incentives to give it can be determined how certain parameters and mechanisms influence contributions. I first review the literature that asks whether giving can be viewed as rational, in the sense that individuals have well-behaved preferences over payoff to self and payoff to others. I then present a series of studies examining both the precise motives for giving and the role error plays in these environments. I also discuss recent work, which questions the extent to which contributions observed in the laboratory or the field can be seen as evidence of an underlying motive for giving or rather as an attempt to signal a particular motive for giving, be it as a signal to oneself or to others (self-signaling versus social signaling). I conclude the section by trying to reconcile these different interpretations of the data on giving. 2.1 Is Giving Rational? To draw inference on motives, researchers have asked first whether contributions in the laboratory can be viewed as intentional and, second, whether they should be seen as rational. Unfortunately the prediction of zero giving in both the dictator and linear public good (VCM) games implies that positive contributions need not be deliberate. Mistakes made by payoff-maximizing participants can result only in positive transfers, which may be falsely viewed as evidence of other-regarding behavior. The finding that giving in the VCM decreases with experience suggests that errors partially account for initial contributions. The early work on intentions was reviewed by Ledyard (1995) and suggests that while mistakes play a large role, a sizable share of giving is intentional.8 The seminal work by Andreoni and Miller (2002) proceeds by asking whether giving can be viewed as rational. That is, is behavior consistent with utility maximization and can it be captured by a well-behaved preference ordering? To test if behavior follows the neoclassical principles of revealed preference, Andreoni and Miller give participants several opportunities to transfer part of an endowment at varying prices to an anonymous partner. Participants in this extended dictator game are presented

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with 8 (or 11) budgets of the following format “Divide 60 tokens: Hold_____ at 1 point each, and Pass______ at 2 points each” (that is, the endowment is 60 tokens, a token held is worth 1 point to the decision maker, and a token passed is worth 2 points to the anonymous partner). Securing a large number of intersections between the budgets it is then determined if a participant’s choices satisfy the generalized axiom of revealed preference (GARP). Surprisingly 98% of participants make choices that are consistent with utility maximization; hence the observed transfers can be generated by a continuous, convex, and monotonic utility function over payoff to self and payoff to others. To assess the power of the test, Andreoni and Miller ask how difficult it would be to violate GARP in the examined environment. They rely on both an ex ante and ex post evaluation. The ex ante test is that of Bronars (1987) and it compares the frequency of violations of the axioms of revealed preferences to that of a synthetic individual, who randomly selects an allocation on any given budget. Relying on uniform draws, the test does not take into account the participants’ transfers in the study. In an ex post test, they therefore look at the violations that result when a synthetic individual draws from the set of transfers selected by participants in the study. They find in contrast to actual behavior that the vast majority of these ex ante and ex post synthetic individuals violate GARP, and they conclude that contributions in the dictator game can be viewed as rational.9 Fisman, Kariv, and Markovits (2007) replicate the results of Andreoni and Miller (2002) when using a graphical interface to elicit choices over a substantially larger set of budgets. Each participant in their experiment is asked to make decisions over 50 randomly selected budgets. The participant is given a graphical representation of each budget over payoffs to self and payoffs to an anonymous partner; they are then asked to point and click on a preferred allocation in the budget set. Similar to Andreoni and Miller, choices are by and large shown to be consistent with utility maximization. First, half of the participants make choices that fully exhaust the budget, with the number increasing to 84% when allowing for a 5-token margin.10 Second, while the number of violations of GARP increases relative to Andreoni and Miller, this increase is to be expected given the larger number of budgets. Importantly, the observed violations become consistent with utility maximization if one allows for only minor adjustments in the participant’s budgets.11 Fisman and others also examines the ex ante Bronars’ test and find that participants make many fewer mistakes than predicted for synthetic individuals who randomize among the allocations on the budget set. Similar to Andreoni and Miller, they conclude that contributions are consistent with a wellbehaved utility function. Evidence suggests that these results also hold when there is more than one recipient. Andreoni (2007) finds that with two recipients rather than one, it continues to be the case that there are only a few GARP violations. Furthermore doubling the number of recipients increases total giving but does not double it; thus the average contribution to an individual decreases as the size of the group grows. Fisman, Kariv, and Markovits (2007) also examine transfers to two recipients. They find only a marginal increase in total giving relative to the one-recipient case.12 As Andreoni (2007), they find few and small violations of GARP and conclude that transfers are consistent with utility maximization. In sum, laboratory studies find that transfers respond to changes in the environment in a manner that is consistent with the individual maximizing utility over payoff to self and payoff to others.13 As choices can be seen as intentional and rational, it is thus reasonable to ask what these preferences look like and what motivates charitable giving more broadly.

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2.2 Motives The motives for other-regarding behavior have received substantial attention over the past two decades. Cooper and Kagel (Chapter 4) review the insights that have been gained from the literature on concerns such as fairness and reciprocity. The emphasis here is on unconditional transfers, as these correspond to donations for which there is no apparent material motive for giving.14 Consistent with Figure 2.1, unconditional transfers, such as charitable giving, were initially modeled as being motivated by pure altruism. Theoretical investigations soon revealed that pure altruism generates predictions that differ from the charitable giving behavior typically observed in the field. The predictions that have gained most attention are those of complete crowd-out and extreme free riding. Both result from the altruist’s sole motive being the desire to increase the nonprofit’s output and therefore viewing giving by others as a perfect substitute for giving by self.15 Perfect substitutability implies that an increase in government provision funded by lump-sum taxes fully crowds out individual contributions, as the individual decreases his or her donation by precisely the amount of the lump-sum tax. Similarly, as shown by Andreoni (1988a), perfect substitutability implies that in the limit as the population gets large, there will be extreme free riding, and only those who care most for the public good and have the highest income will contribute.16 To develop a model with comparative statics that mirror those of the field, it was argued that donors also receive a private benefit or warm-glow from giving (Andreoni 1989, 1990).17 That is, the act of giving generates a benefit that does not depend on the effect the donation has on the nonprofit’s output or on the recipients’ well-being.18 Individuals motivated solely by warm-glow will, therefore, not respond to changes in giving by others, and those who are motivated by both altruism and warm-glow (impure altruists) will view giving by others as an imperfect substitute for giving by self. Assuming that warm-glow is perceived as a normal good and that it is operative at all levels of provision, this model of impure altruism eliminates the complete crowd-out and extreme free-riding predictions of the pure altruism model. Much research has been done to determine the extent to which giving is explained by a concern for the welfare of others (altruism), warm-glow from giving, or error. Although the objective ultimately is to determine motives for giving in the field, a natural starting point has been to look at motives in the laboratory.19 Researchers have relied on two methods of identification: one alters the cost and benefit from giving in the VCM and the other tests the crowd-out predictions that result from pure and impure altruism models of giving. Studies using these two methods are discussed next. 2.2.1 ALTRUISM, WARM-GLOW, OR NOISE: CHANGING THE COST AND B ENEFIT FROM G IVING To examine motives for giving, we may alter the incentive to give in the VCM. However identification requires more than a simple change in parameters. When transferring an endowment from a private account with a return of r to a public account with a return of m, a higher marginal per capita return (MPCR = m/r ) both increases the return others get from the transfer and decreases the individual’s cost of making the transfer. Thus an increase in the MPCR is predicted to increase giving for a pure altruist, for a pure warmglow giver, and for someone who is more prone to make errors when it is cheaper to do so. Slight modifications of the VCM payoffs, however, make it possible to separate the cost and return from giving, and thereby identify what likely motivates giving.20

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Palfrey and Prisbrey (1997) consider a partner design where participants are matched with the same group for ten rounds and then matched with a new group for each of three subsequent segments of 10 rounds. The return from the public good, m, is common knowledge and is the same for all members of the group. Deviating from the standard VCM they let the cost of contributing, r i , vary by individual. The distribution of r i is commonly known, but the individual’s actual return is private information. Individual payoffs are given by: πi = r i (w − g i ) + m

n 

gj

j =1

Mistakes may result in both over- and undercontributions in this environment. When m/r i < 1, it is a dominant strategy to give nothing, and when m/r i > 1, it is a dominant strategy to give everything. Furthermore, when m/r i < 1/n, it is inefficient to contribute to the public good. By varying r i , it is thus possible to determine whether a contribution was a mistake and to determine what type of preferences best capture behavior. To account for the fact that data may be noisier when it is cheap to make mistakes, Palfrey and Prisbrey use a quantal response model of equilibrium behavior to estimate preferences. While examining both nondivisible and divisible endowment transfers, they estimate a linear utility function where participants are predicted either to give or not to give to the public good.21 They find, as studies before them, that contributions decrease over the course of the experiment, and their empirical analysis suggests that this decrease is partially attributed to a decrease in mistakes. They also find that contributions decrease with the cost of giving and increase with the return to the public good. The latter effect is, however, not significant. Palfrey and Prisbrey conclude that there is strong and substantial evidence that giving is explained by warm-glow and error, but not by altruism.22 The finding that giving is not motivated by altruism differs, however, from that of other studies. Anderson, Goeree, and Holt (1998) examine data from the linear VCM studies by Isaac and Walker (1988) and Isaac, Walker, and Williams (1994) and find that contributions increase with the return to the public good and with the population size (provided a not-too-large MPCR). The broad characteristics of these data are seen as indicative of altruism. When estimating preferences, they find significant evidence of both altruism and error but find no evidence of warm-glow. Reexamining the Palfrey and Prisbrey payoff structure, Goeree, Holt, and Laury (2002) note that the return from the public account both increases the return to others and decreases the cost of giving. To separate the dual effect of the MPCR, they allow the return from the public good to vary between self and others. Contributions generate an internal return, mi , to the decision maker and an external return, me , to the other members of the group (Carter, Drainville, and Poulin (1992) use a similar payoff structure). That is, the payoff from contributing is given by πi = r (w − g i ) + mi g i + me



g j.

j =i

Goeree and others ask participants to make a series of 10 decisions. In each decision the participant is asked to allocate 25 tokens between a public and private account.

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Tokens contributed Internal return = 4 20

Internal return = 2

15 10 5 0

N=4 N=2 2

4

6

2 4 External return

6

8

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Figure 2.2: Average contributions out of 25 tokens by return to giving (external and internal) and by group size (n = 2, 4). Source: Reprinted from Jacob K. Goeree, Charles A. Holt, and Susan K. Laury, “Private Costs and Public Benefits: Unraveling the Effects of Altruism and Noisy Behavior,” Journal of Public Economics 83, no. 2 (2002): 255–76, Copyright 2002, with permission from Elsevier.

Decision problems vary both the internal and external return as well as the number of people in each group. The parameters of each decision problem are common knowledge and chosen to preserve the character of the standard VCM. That is it is not payoff maximizing for the individual to give, and efficiency is achieved through full provision. With no feedback between decisions participants effectively make ten oneshot decisions. As seen in Figure 2.2, the primary results by Goeree and others replicate the finding that contributions increase with the internal return mi (decreasing costs); however, consistent with altruism they also find that contributions increase in the external return me and with the size of the group (N). The response to the external return of giving suggests that a pure warm-glow specification fails to capture behavior. Using a Logit probabilistic choice function, they estimate the participants’ preferences for giving. In comparing the pure altruism and pure warm-glow model, they find that pure altruism has greater explanatory power. Furthermore, when estimating an impure altruism model where individuals benefit both from the return to others and from the donation itself, they find that the coefficient on warm-glow has the wrong sign and is insignificant. Asking the same question and using similar designs and methodologies, Palfrey and Prisbrey and Goeree and others reach strikingly different conclusions. Palfrey and Prisbrey find evidence of warm-glow and noise, while Goeree and others find evidence of altruism and noise. Seemingly small design differences may have contributed to the different results. Although both estimate preferences over one-shot payoffs, the Palfrey and Prisbrey study is, instead, a partner design where participants are paired for a total of ten periods. What appears to be a decision error in their study may instead result from the participants’ attempts to sustain contributions over the finitely repeated game. Failure to contribute when it is payoff maximizing to do so need not result from error but may be instead an attempt to punish others. Similarly, the decision to make a costly contribution may result from an attempt to reward or sustain cooperation. Another suggested reason for the difference between the two studies is that the cost

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of giving is heterogeneous and private information in the Palfrey and Prisbrey study. This uncertainty over cost may have provided participants with moral wiggle room and an “excuse” for low contributions, and this may in turn have decreased giving.23 Note, however, that Palfrey and Prisbrey (1993) find no significant effect of letting the cost of contributing be commonly known. 2.2.2 ALTRUISM, WARM-GLOW, OR NOISE: CROWDING OUT Another method frequently used for separating the altruistic and warm-glow motives for giving builds on the empirical approach used when examining secondary data.24 Specifically, it tests the crowd-out prediction of the alternative models of charitable giving. Crowd-out for pure altruists is predicted to be complete when an increase in government giving is funded through a lump-sum tax. By contrast, a model of warmglow giving predicts only an income effect from a lump-sum tax. Finally, the impure altruism model, where individuals are motivated both by altruism and warm-glow, predicts that the degree of crowd-out lies between that of the pure-altruism and warmglow models. Andreoni (1993) develops an early experimental test of the crowd-out hypothesis. Groups of three participants are randomly formed every fourth round and are in each round asked to contribute to a public good. Deviating from the linear VCM, Andreoni uses a Cobb-Douglas payoff structure to secure that both the predicted equilibrium and the Pareto efficient outcome are interior to the strategy space. Two treatments are compared: a no-tax and a tax treatment. The payoffs of the two treatments are shown in Table 2.1. Contributions are described as investments and each cell reports the individual’s earnings given his or her contribution and the sum of contributions by the two other group members. Looking first at the no-tax treatment in panel a, the symmetric Nash equilibrium of the game is for each participant to contribute 3 tokens and the efficient outcome is for each participant to contribute 6 tokens. The Cobb-Douglas payoff structure eliminates equilibria in dominant strategies and participants may select contributions that are dominated from an individual as well as an other-regarding perspective. With participants in the no-tax treatment being free to contribute any amount between 0 and 7, Andreoni captures the effect of a lump-sum transfer to the public good by imposing an initial contribution of 2 tokens and giving participants the option of adding between 0 and 5 tokens to this initial level of giving. Payoffs in the tax treatment (panel b) are simply a truncated version of those in the notax treatment, and the equilibrium prediction is for everyone to contribute one token. If individuals are purely altruistic, the 2-token tax will be crowded out completely and contributions in the tax treatment are predicted to be 2 tokens smaller than those in the no-tax treatment. If, however, a participant benefits from being the one who voluntarily contributes to the public good, that is, the individual receives a warm-glow from giving, then the forced contribution is an imperfect substitute for giving by self and crowd-out will be incomplete. Comparing giving between the tax and no-tax treatment, Andreoni finds an average crowd-out of 71.5% over all rounds of the game and a crowd-out of 84% in the last round of the game.25 Both these measures differ significantly from the 100% crowd-out predicted by the pure altruism model. Andreoni concludes that behavior is consistent with participants being impure altruists. Bolton and Katok (1998) extend the crowd-out examination to the dictator game, where a decision maker is informed of an initial exogenous transfer to an anonymous

0 1 5 12 21 34 49 68 90 115 143 175 210 248 290

Your Investment 2 3 4 1 3 6 9 4 8 11 14 9 14 18 20 17 22 26 28 28 33 36 37 40 45 48 47 56 60 61 59 74 77 76 72 95 96 93 86 118 117 111 102 144 140 131 119 173 166 153 137 205 193 177 157 239 223 203 178 276 256 230 201 Panel a: No-Tax Treatment 1

5 10 15 21 28 35 44 54 64 76 89 103 118 134 151 169

6 11 15 20 25 32 39 47 55 64 74 85 97 109 122 136

7 10 14 17 22 27 32 38 44 51 58 66 75 84 93 103 0 1 2 3 4 5 6 7 8 9 10

0 33 45 60 77 96 117 140 166 193 223 256

Your Investment 1 2 3 4 36 37 35 32 48 47 44 39 61 59 54 47 76 72 64 55 93 86 76 64 111 102 89 74 131 119 103 85 153 137 118 97 177 157 134 109 203 178 151 122 230 201 169 136 Panel b: Tax Treatment 5 27 32 38 44 51 58 66 75 84 93 103

Source: James Andreoni, “An Experimental Test of the Public-Goods Crowding-Out Hypothesis,” American Economic Review 83, no. 5 (1993): 1317–1327. Copyright American Economic Association; reproduced with permission of the American Economic Review.

Total Investment by the Other Two Group Members

0 1 2 3 4 5 6 7 8 9 10 11 12 13 14

0

TABLE 2.1: Individual payoff by individual and group investment.

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recipient and given an endowment, which the decision maker may keep or use to increase the recipient’s transfer. The central comparison is once again between transfers in a tax and a no-tax treatment. In the no-tax treatment, the exogenous transfer to the recipient is $2 and the decision maker’s endowment is $18; in the tax treatment the exogenous transfer to the recipient is instead $5 and the decision maker’s endowment is $15. That is, the tax treatment captures the effect of a $3 lump-sum tax. Under pure altruism and complete crowd-out, individuals who give more than $3 in the no-tax treatment are predicted to decrease contributions by $3 in the tax treatment. Comparing average transfers in the tax and no-tax treatment, Bolton and Katok find that 73.7% of the “tax” is crowded out.26 As did Andreoni (1993), they fail to find evidence of complete crowd-out and conclude that giving is explained by impure altruism. Eckel, Grossman, and Johnston (2005) extend Bolton and Katok’s study by considering transfers to real charities, that is, they replace the anonymous recipient of the dictator game with a charity of the participant’s choice. They examine the degree of crowd-out using two different types of framing. The first neutral frame mirrors that of Bolton and Katok, where participants simply are informed of the initial allocation ($18/$2 or $15/$5). The second tax frame instead informs participants that a $2 or $5 tax was imposed on their initial $20 endowment and that the money will be given to the charity of their choice. Framing is shown to have a substantial effect. In the neutral frame they observe essentially no crowd-out, and in the tax-frame they find complete crowd-out. When participants are made aware of the tax, the evidence is consistent with pure altruism.27 Common for these crowd-out studies is that they elicit one measure of crowdout and that incomplete crowd-out is seen as evidence of impure altruism. OttoniWilhelm, Vesterlund, and Xie (2014) point to limitations of this approach. Revisiting the asymptotic results by Ribar and Wilhelm (2002), they first show that under the impure altruism model the degree of crowd-out will depend on where it is elicited. As the initial exogenous contribution to the recipient (or charity) gets sufficiently large, the individual’s marginal motive for giving will shift from one of impure altruism to one of pure warm-glow, and the degree of crowd-out will decrease. Hence the power to reject pure altruism depends on the provision at which the test is conducted. Furthermore, with crowd-out changing, a single measure of crowd-out cannot identify the relative importance of warm-glow preferences. In determining the weight on warmglow relative to that on altruism, infinitely many weights can explain any incomplete measure of crowd-out, ranging from almost pure altruism to pure warm-glow. Hence, it is necessary to measure crowd-out around more than one level of provision to identify the relative concern for warm-glow and altruism. Ottoni-Wilhelm, Vesterlund, and Xie (2014) also argue that since the impure altruism model was designed to reconcile theory with preexisting field evidence of incomplete crowd-out, we cannot see evidence of incomplete crowd-out as a test of impure altruism. In designing a direct test of the impure altruism model they note that the model predicts that crowd-out decreases as the amount given by others increases. Hence they uncover a testable comparative static of the impure altruism model that it was not designed to have. Examining the sensitivity to the amount of giving by others, they introduce a new experimental design that controls the level of giving by others and use it to estimate crowd-out at a low and a high provision level. Creating what they refer to as an individualized charity, they secure that each participant effectively contributes to an individualized public good and singlehandedly determines the total provision of that

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TABLE 2.2: Experimental budgets.

Budget 1 2 3 4 5 6

Fixed Initial Donation (G −i )

Participant’s Endowment (wi )

4 10 28 34 4 28

40 40 40 40 46 46

Source: Reprinted from Mark Ottoni-Wilhelm, Lise Vesterlund, and Huan Xie, “Why Do People Give? Testing Pure and Impure Altruism” (working paper), with permission from the authors.

good. Specifically, each participant is paired with a child who has just lost his or her home in a fire. The participant in the study is asked to make a contribution that will be used to purchase books for the child. These books are to be given to the child by the American Red Cross as they arrive at the scene of the fire to assist in relocating the family. To determine the response to the amount given by others, the participant is asked to make a number of decisions. For each decision they are informed how much the child is to receive absent the participant’s contribution, and they are given an endowment, which they are free to contribute towards books for the child. As no other gifts are given to the child at the scene of the fire, only the participant can influence the total value of the books to be transferred to the child. The six budgets examined are shown in Table 2.2. The degree of crowd-out in response to a $6 lump-sum tax is determined both at a low provision level of $4 (budgets 5 and 2) and at a high provision level of $28 (budgets 6 and 4). Unfunded crowd-out at a low and high provision level is measured between budgets 1 and 2 and between budgets 3 and 4. Finally, the corresponding income effects are measured between budgets 1 and 5 and between budgets 3 and 6. The experiment provides the first evidence that crowd-out depends on the level of giving by others at which crowd-out is measured. At the low level of giving by others, crowd-out is essentially complete, but at the high level it is incomplete. If only one measure of crowd-out had been elicited, the inference on motives at the low level would have been one of pure altruism, while at the high level it would have been one of impure altruism. Importantly, the results reveal that the decrease in crowd-out is statistically significant, thus confirming the comparative static prediction of the impure altruism model. With behavior consistent with impure altruism, they estimate preferences for giving. While confirming that in addition to the altruism component, the warm-glow component of utility is necessary to explain the experimental data, the structural model indicates that the weight placed on warm-glow is small. The study demonstrates that for the charity in question giving is motivated primarily by altruism. Inference from crowd-out studies have not been limited to looking at transfers. A study by Harbaugh, Mayr, and Burghart (2007) use fMRIs to draw inference on motives. They compare neural activation in two different treatments. Individuals in a no-tax treatment are given $100 and asked whether they are willing to make a specific transfer to a local charity; in a tax treatment, the transfer is instead mandatory. Consistent with altruism, they find that an increase in funding for the charity elicits neural activity in areas linked with reward processing (increases in one’s own payoff and in the charity’s payoff increase activation in similar areas of the ventral striatum).

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Based on the relative activation seen when none or all the money is transferred, they sort participants into a more and less altruistic half. As evidence that the observed activation is predictive of behavior, they find that the more altruistic half is twice as likely to accept proposed transfers to the charity. Consistent with impure altruism, they observe an increase in neural activity (higher activation in the caudate, the right nucleus accumbens, and the insulae) when moving from the tax to the no-tax voluntary treatment. This pattern of neural activation, combined with the fact that participants report greater satisfaction with the voluntary manipulation, lead the authors to conclude that both altruism and warm-glow explain charitable giving.28 Through careful experimental designs recent work has improved our ability to identify motives for giving. What we have not achieved, however, is broad agreement on what these motives are. Some studies find that giving primarily is driven by warmglow; others find that it is driven by altruism and others that it is affected by both. To some extent these inconsistencies should not be surprising. First, as shown by OttoniWilhelm, Vesterlund, and Xie (2014), the marginal motive for giving changes with the initial funding of the public good, and variation in provision provides a possible explanation for the varied inference on motives. Second, the underlying preferences for giving are likely to depend on what the funds are solicited for. In fact, in examining donations to nonprofits or recipients outside the laboratory, it is unlikely that consensus on motives can or should be reached. Just as the demand for one private good does not predict the demand for all other private goods, it is not to be expected that the demand— or the motive for such a demand—is the same for all generous acts. While altruism may drive giving to a charity such as the Red Cross, warm-glow may be what causes people to give to an already well-endowed alma mater such as Harvard.29 Rather than seeing the examined experimental studies as an attempt to uncover a general preference for giving, it may be useful to see them as developing techniques that make it possible to determine what motivates giving to a particular charity. 2.2.3 IS EVIDENCE OF KINDNESS A RESULT OF KINDNESS? Further complicating our ability to draw inference on motives is a recent strand of the literature that argues that transfers in the lab and in the field do not reflect preferences for others but rather the desire to be perceived as if one has such preference. Researchers have most commonly examined this hypothesis by modifying the experimental environment in ways that should not influence behavior given the initially inferred preferences. Two general modifications have been examined. The first provides participants with a chance to opt out of the giving environment. The second weakens the inference others can draw on the individual’s type.30 Donations motivated solely by concern for others should not respond to either of these modifications. Yet, as evidence that the inference on motives may be misleading, both of these changes have been shown to decrease giving. I first look at the effect of offering participants a choice or an excuse to opt out of being informed of or being in the donation environment. Dana, Weber, and Kuang (2007) compare two treatments where a decision maker is paired with an anonymous recipient and selects between two allocations of payoff-for-self and payoff-for-other, (πs , πo ). In one treatment the choice is between (πs , πo ) = ($6, $1) and ($5, $5). In the second treatment the decision maker also selects between getting $6 and $5 for self; however, he or she does not know what the associated payoff is for the recipient. That is, the choice is between ($6, π o ) and ($5, πo ), where the recipient’s associated payoff,

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πo and πo , is determined by a coin flip prior to the session and equals either $1 or $5. While not informed of the exact payoff consequences for the recipient, the decision maker has the option of clicking a button to resolve the uncertainty. Interestingly, 43% of decision makers do not click the button, and under this “veil of ignorance” they are more likely to choose the allocation with $6 for self. The choice of ($6, $1) increases from 26% to 63% when the $1 payoff consequence is not revealed. It is as if the perceived randomness provides moral wiggle room to be selfish. A similar effect is seen in Dana, Cain, and Dawes (2006), where a decision maker can opt out of the dictator game. Having made a transfer decision in a $10 dictator game, the decision maker is informed that there is an option of reneging on the planned transfer and instead receiving $9. If the opt-out is selected, the recipient never learns that the dictator game was an option. Although the opt-out is costly, they find that a third of participants select it.31 As evidence that initial transfers result from a desire not to violate others’ expectations, they show that only 4% of participants opt out when the recipient never learns that a dictator game is played. This elimination of responsibility is also seen in Hamman, Lowenstein, and Weber (2010). They find that while dictators on their own make generous transfers, when asked to delegate the allocation decision to an agent, they select an agent who makes a minimum or no transfer to an anonymous recipient.32 The chosen agent implements allocations that are far less generous than the allocations they would have selected on their own. The finding that transfers decrease when there is an option to opt out suggests that the transfers seen absent this option do not solely reflect a concern for the well-being of others. Further evidence that it is difficult to identify motives is seen in the many studies that find contributions to be sensitive to the inference others may draw on the donor’s type. Transfers in the dictator game are commonly found to decrease when it is difficult to link the individual’s decision to her identity. Hoffman and others (1994) and Hoffman, McCabe, and Smith (1996) investigate a double-blind dictator game where neither the recipient nor the researcher is able to identify the decision maker. They find that this increase in social distance decreases giving to a mere 10% of endowments. At the opposite end of the spectrum, Bohnet and Frey (1999) find that contributions increase in one-on-one interactions. Visibility has also been shown to increase generosity in the VCM.33 Rege and Telle (2004) conduct a one-shot VCM where participants, after making their contribution decisions, are asked, one person at a time, to step forward to announce their decisions. Contributions increase when they are publicly announced. Andreoni and Petrie (2004) also examine visibility in the VCM. Participants are paired in groups of five for eight rounds, and the experiment manipulates the information given on the contributor and his or her decision. They find that information on contributions increase giving, but only when it is combined with a picture of the individual contributing.34 To better understand the effect of visibility, Ariely, Bracha, and Meier (2009) conduct an experiment to test a model of image motivation proposed by Bénabou and Tirole (2006). They conduct two types of real-effort experiments where effort generates contributions to nonprofits: click for charity and bike for charity. The receiving nonprofit was either “good” or “bad” (Red Cross and National Rifle Association, respectively).35 Manipulating the visibility of the exerted effort as well as whether the participant is compensated for effort, they determine when and why visibility influences behavior. The results of the click for (a good) charity task are shown in Figure 2.3. For this task participants have 5 minutes to sequentially press two keys (X and Z). For every completed pair of clicks, a donation is made to the nonprofit. For this good cause they

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1,200 Private

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800 600 400

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1,000

1,000 Number of keypresses

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Without With incentive incentive Payment scheme Panel a: “good” cause

0

Without With incentive incentive Payment scheme Panel b: Red Cross

Figure 2.3: The effect of incentives on prosocial behavior when behavior is visible (public) versus not visible (private). Source: Dan Ariely, Anat Bracha, and Stephen Meier, “Doing Good or Doing Well? Image Motivation and Monetary Incentives in Behaving Prosocially,” American Economic Review 99, no. 1 (2009): 544–55. Copyright American Economic Association; reproduced with permission of the American Economic Review. Notes: Error bars are standard errors of the mean. Panel A shows effort for a “good” cause according to individual participant’s perception of other students’ identification at Princeton. Panel B shows effort for the Red Cross (the majority of Princeton undergraduates positively identifies with this charity).

find that visibility increases giving and that extrinsic motivation reduces the image signal of giving when behavior is visible. That is, effort decreases for the good cause in the visible treatments when participants are financially compensated for effort. By contrast, a monetary compensation causes individuals to increase their effort when performing in private. This suggests that extrinsic incentives decrease the image effect when giving in public. For the bad cause, they find instead that monetary compensation for effort does not affect contributions in public and increases them in private. The results are similar for the bike-for-charity task, and they interpret their findings as providing evidence that giving is motivated by concerns for image. Related to the evidence on social distance and visibility are studies that modify the environment to alter the norm for giving and thus the signal one sends by giving. For example Bardsley (2008) and List (2007) examine contributions in a dictator game where the strategy space is modified to allow for the option of taking from the recipient.36 Both studies find that contributions decrease substantially when taking is permitted. Furthermore, List shows that contributions decrease even further when the number of tokens that may be taken increases. Both authors argue that the response results from it being cheaper to signal generosity when there is an option of taking. While a zero transfer is seen as selfish in the standard dictator game, it may be seen as generous in the “taking” game. The ability to draw inference on generosity has also been shown to influence behavior. For example Andreoni and Bernheim (2009) develop a signaling model where

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0.8 0.7

Fraction

0.6 0.5 0.4 0.3 0.2 0.1 0

0%

25% 50% Probability of forced choice, x0 = 0

75%

Figure 2.4: Frequency of amount allocated to partners conditional on the probability of a forced choice. (a) Forced choice is 0. (b) Forced choice is 1. Source: James Andreoni and B. Douglas Bernheim, “Social Image and the 50–50 Norm: A Theoretical and Experimental Analysis of Audience Effects,” Econometrica 77, no. 5 (2009): 1607–36. Printed with permission of the Econometric Society.

the desire to be perceived as fair causes donors to select the focal 50–50 split in the dictator game. They conduct a series of $20 dictator games in which, with a certain probability (0%, 25%, 50%, 75%), the computer overrules the dictator’s choice and forces a low transfer of either $0 or $1 to the recipient. Figure 2.4 summarizes their results. When the probability of a forced transfer is 0, they find, as others before them, a modal 50–50 split. However as the probability of a forced low transfer increases, transfers deviate from the 50–50 split and become the amount that could have been forced. As the probability of a forced choice increases we see an increase in the frequency of a chosen $0 transfers in panel a and an increase in the frequency of a chosen $1 transfers in panel b. Evidence of the desire to signal generosity has also been examined in the field. DellaVigna, List, and Malmendier (2012) conduct a field experiment to examine the role social pressure plays in securing donations. In a door-to-door fundraising experiment, they compare three different solicitation mechanisms: a baseline where households simply are asked to give, a flyer treatment where households receive flyers on their doorknobs one day in advance of the solicitation to notify them of the 1-hour time interval in which a solicitor will arrive at their homes the next day, and, finally, an opt-out treatment where the flyer includes a box to be checked if the household does not want to be disturbed. They find that the share of available households decreases in the treatments with a flyer (10% for the simple flyer and 25% for the flyer with the optout box). Donations are affected in the opt-out treatment only, where a drop in small donations (less than $10) results in a 30% decrease in giving. The authors argue that the decrease in giving in the opt-out treatment demonstrates that giving is driven by social pressure. Estimating preferences, they conclude that social pressure plays a greater role than altruism in motivating giving. In fact, they suggest that the impact of social pressure is so large that door-to-door fundraising is welfare reducing.

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The studies reported here make clear that contributions are sensitive to the characteristics of the environment. Social distance, wiggle room, and visibility all influence giving. However, none of these findings are likely to surprise a trained fundraiser. Those who solicit funds are fully aware that social distance and the possibility of opting out decreases giving. This is why resources are spent to secure a direct ask over the much cheaper mail solicitation. Fundraisers would also not be surprised that the strategy space or visibility affects giving; after all they personalize the suggested donation levels and publicly announce contributions to others.37 While it is clear that giving is influenced by a number of factors, it is less clear what implications this has on our inference on motives for giving. Is it necessarily the case that donors who cannot opt out in the DellaVigna, List, and Malmendier (2012) study give because of social pressure? An alternative explanation for opting out may be that the donor has self-control problems. Knowing that he or she is altruistic and will feel compelled to give when asked, the donor may opt out of giving, not to avoid the social pressure but to limit the temptation to give.38 Another reason we should use caution when inferring preferences from the opt-out decision is that preferences themselves may respond to the direct solicitation. Schelling (1968) argued that the more we know about a recipient, the more we care. Thus when surprised by a panhandler and standing face-to-face with him or her, we may care more about his or her well-being than we would have had we crossed the street to opt out of the request for funds. While the opt-out decision should cause us to question our inference on motives for giving, it is less clear that it helps identify what motivates giving when there is no option to opt out. One interpretation of these studies is that it is not possible to draw inference on motives. Bardsley (2008) proposes a more constructive interpretation. He argues that preferences for giving might better be seen as attempts at reasonable approximations of specific motivations over limited domains rather than as general truths. Indeed, the laboratory experiments on giving aim to map the domain individuals face when approached by a solicitor and asked to give. The interest in both the public good and dictator games is driven by the fact that they mirror environments where individuals are asked to give. While it may not be possible to identify preferences for giving that predict transfers in all domains, careful experimental designs allow us to identify the class of preferences that are consistent with the behavior observed in common donation domains. While not providing general truths, these findings will nonetheless provide insights on behavior in the domains of interest.

3 FUNDRAISING The simultaneous contribution game modeled in Section 2 relies on the assumption that individuals on their own and without knowledge of others’ actions decide how much to contribute to a nonprofit. Contributions in the field, however, make clear that a more complex contribution game is in place and that it is strategically chosen by those soliciting funds. Fundraisers may design a campaign where individuals are informed of the behavior of others and asked to contribute at a particular point in time. Or they may opt to hold a charity auction or to alter the donor’s incentive to give, be it by letting contributions generate a gift, tickets in a raffle, or a matched contribution by another donor. Substantial work has been done to characterize and understand what mechanisms fundraisers use to solicit funds and why they might be effective. As noted in

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the introduction, the fundraiser differs from the social planner of the classic mechanism design problem both in objective and in the tools that are available. Specifically, the fundraiser’s objective is assumed to be one of contribution maximization, and he or she must rely on voluntary participation.39 In examining the market for voluntary giving, it is essential that we understand the choices fundraisers make when designing the contribution game. I first discuss research examining the sequential and dynamic nature of voluntary giving. Second, I review the literature on competitive contribution mechanisms such as lotteries and auctions. Finally, I report on studies examining direct benefits such as matches and rebates. 3.1 Announcements: Sequential and Dynamic Giving Fundraising is typically done in a sequential fashion. Potential donors are solicited for funds at a particular point in time and, when asked to give, they are informed of the contributions others have made before them. That is, donors may receive information on the sum of contributions that have been collected to date, the size of a “leadership” donation in a capital campaign, the fraction of potential donors that have contributed thus far, or the funds raised in similar campaigns. There are many channels through which this information can influence behavior. I begin by examining sequential giving and then proceed to more complex dynamic environments where donors have multiple opportunities to give and contributions at any point in time are made simultaneously. 3.1.1 SEQUENTIAL GIVING At first sight the fundraiser’s reliance on sequential giving seems puzzling. Varian (1994) compares a simultaneous contribution game to one where donors contribute in sequence after being informed of the decisions of others. He demonstrates that the latter is likely to reduce provision. With altruistic preferences, sequential giving enables the initial donor to free ride off of subsequent donors. Thus provision in the sequential game is predicted to decrease relative to that in the simultaneous game. Varian’s result demonstrates that it is not obvious why fundraisers solicit sequentially. However concerns for both equality and reciprocity may cause behavior to differ from that predicted. To investigate the role of these factors, experimental studies have examined the simple two-person quasi-linear example provided by Varian. The quasi-linear environment gives rise to the stark prediction that with heterogeneous preferences, only one person contributes. The person with the strongest preference for the public good is predicted to be the sole contributor in the simultaneous game, and the person with the weakest preference is predicted to be the sole contributor when he or she is the second mover in the sequential game (provided a not-too-large difference in preferences).40 With sequential giving the first mover gives nothing and the second mover contributes an amount that is no larger than that contributed in the simultaneous game. Examining a two-person quasi-linear environment, Andreoni, Brown, and Vesterlund (2002) confirm the comparative static prediction that contributions are larger in the simultaneous than in the sequential game.41 However, in contrast to the equilibrium prediction, they do not find that contributions are made

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by only one player; rather the burden is shared close to equally between the two. The absence of a substantial first-mover advantage is explained by the second mover’s unwillingness to contribute unless the first mover does so as well. Gächter and others (2010) expand on these findings. Examining a similar environment, they replicate for a more extreme set of parameters the findings that contributions are lower under sequential than simultaneous moves and that the contribution distribution is not as unequal as predicted. First movers are unable to secure their predicted first-mover advantage. Interestingly, unequal contribution distributions are seen when the first mover’s preference for the public good is so strong that he or she is predicted to be at a disadvantage and to be the sole contributor. Gächter and others interpret the two findings as resulting from the second movers’ willingness to punish first movers who free ride and unwillingness to reward first movers who contribute. With evidence of lower giving in the sequential game, the question remains why fundraisers announce past contributions to future donors.42 A number of studies examine field-relevant modifications of Varian’s model to determine whether these help generate predictions consistent with the preference for sequential play. One explanation is provided by Andreoni (1998), who shows that sequential solicitations may be preferred when there are fixed costs of production. When no individual singlehandedly is willing to cover the fixed costs, simultaneous giving may result in both positive and zero-provision equilibria. Thus campaigns that rely on simultaneous giving may get stuck in an equilibrium, where donors fail to coordinate on a preferred positive provision outcome. Such inferior equilibria are eliminated when contributions are made sequentially. The reason is that a large initial “seed” contribution indicates that the fixed costs can be covered, and this in turn causes followers to give and secure provision of the public good.43 Vesterlund (2003) provides a second explanation for sequential solicitations. Examining a model where the quality of the charity is uncertain, she shows that sequential play helps reveal the quality and in so doing increases provision. Sequential play is consequently selected in equilibrium. While a fundraiser’s endorsement of a nonprofit is not a credible signal on quality, a large initial contribution is. The signal associated with the initial contribution encourages lead donors to inspect the charity and to contribute an amount large enough to trigger contributions from followers when the quality is high.44 With a simultaneous solicitation strategy serving as a low-quality signal, fundraisers have no option but to solicit sequentially. Furthermore as the first contribution serves as a signal on quality, larger initial contributions secure that giving to high-quality charities exceed those that would result had the quality been common knowledge.45 A third explanation for sequential giving is that donor preferences depend on more than the consumption of the private and public good. Romano and Yildirim (2001) characterize the types of preferences that give rise to greater contributions under sequential play. They show that sequential play is preferred when initial contributions trigger a sufficiently large increase in contributions by followers, and leaders in response give more in the sequential game. For example, giving increases with sequential moves when individuals adhere to Sugden’s (1984) principle of reciprocity, when donors are conformists (Bernheim 1994) and dislike effort differentials (Huck and Rey-Biel 2006), or when donors are concerned about status and follow the lead of high-status donors (Kumru and Vesterlund 2010). The experimental examinations of these three possible explanations for sequential giving are many. List and Lucking-Reiley (2002) present an early study of behavior

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TABLE 2.3: Contributions as a function of an initial seed donation (10%, 33%, or 67% of the $3,000 cost) and the offer of a refund (R). 10

10R

33

33R

67

67R

Number of solicitations mailed Seed money (%) Seed money ($) Refund?

500 10% $300 N

500 10% $300 Y

500 33% $1,000 N

500 33% $1,000 Y

500 67% $2,000 N

500 67% $2,000 Y

Number of contributions Participation rate

17 3.4%

20 4.0%

33 6.6%

31 6.2%

42 8.4%

40 8.0%

Total contributions

$202

$379

$805

$863

$1,485

$1,775

$11.88 $2.27

$18.95 $3.13

$24.39 $2.50

$27.84 $4.59

$35.36 $2.26

$44.38 $6.19

Mean amount given Std error of mean amount

Source: John A. List and David Lucking-Reily, “The Effects of Seed Money and Refunds on Charitable Giving: Experimental Evidence from a University Capital Campaign,” Journal of Political Economy 110, no. 1 (2002): 215–33. Published by University of Chicago Press. © 2002 by The University of Chicago. All Rights Reserved.

in the sequential game and determine whether seed money increases subsequent contributions.46 Using a field experiment they solicit funds to purchase a $3,000 computer for the University of Central Florida Environmental Lab. Potential donors are solicited by mail to contribute toward one of six computers in a 3 × 2 design varying the fraction of the cost that has already been contributed toward the computer (10%, 33%, or 67%) and varying whether contributions short of the goal are refunded to the donor. The interest in refunds is motivated by Bagnoli and Lipman’s (1989) finding that refunds can eliminate the coordination problem in a threshold provision problem.47 To the extent that seed gifts serve as a coordination device, as suggested by Andreoni (1998), this effect is expected to be reduced (if not eliminated) when contributions short of the fixed costs are refunded.48 The central results of the List and Lucking-Reiley study are reported in Table 2.3. As evidence that sequential play may be beneficial, they find that followers appear to have upward-sloping best-response functions. The likelihood of contributing as well as the average contribution increase with the size of the seed gift. Increasing the seed gift from 10% to 67% of the total cost increases contributions sixfold. Surprisingly the effect of the seed gift is independent of the offer of a refund (denoted by R in Table 2.3). As refunds eliminate the coordination problem, the insensitivity to refunds suggests that the increase in giving cannot solely be explained by the coordinating role of a large seed. The increase in giving is however consistent with signaling along the lines of Vesterlund (2003). With and without a refund, a larger seed may be seen as evidence that the nonprofit is of high quality. Similarly, the insensitivity to refunds is also consistent with the positive response to seeds resulting from preferences, along the lines suggested by Romano and Yildirim (2001). While the field study by List and Lucking-Reiley (2002) demonstrates that a large initial contribution increases subsequent giving, it is more difficult to determine what gives rise to the effect. An advantage of laboratory studies is that manipulations of the environment allow us to test the comparative static predictions of the three proposed explanations for sequential solicitations.

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For example, the key insight by Andreoni (1998) is that sequential giving can play a coordinating role when fixed costs are so high that coordination fails under simultaneous giving. A test of this hypothesis requires that the effect of sequential giving is examined for different fixed costs. However, in the field it is difficult to vary the fixed costs of production while keeping other aspects of the environment constant.49 Bracha, Menietti, and Vesterlund (2010) instead use the laboratory to test the coordinating role sequential giving plays under varying fixed costs.50 They examine a two-person public good game with piecewise linear payoffs where there is an interior equilibrium in dominant strategies and an interior Pareto optimal outcome.51 Participants are given an endowment of 10 tokens that they may invest in a public good. The 2 × 3 design varies the sequence of moves (sequential and simultaneous) and the fixed costs of giving (no cost; low cost, 6; high cost, 8). As in Andreoni (1998), the return from the public good arises only when contributions are sufficient to cover the fixed costs. Following Potters, Sefton, and Vesterlund (2005, 2007), sequential and simultaneous giving is implemented by varying whether the second mover is informed of the first mover’s action—that is, both games are “sequential” in moves and only information on the first mover’s choice varies by treatment.52 Consistent with Andreoni’s model, they find that the sequential game can help overcome coordination problems that arise in the simultaneous game. Specifically with high fixed costs (8), individuals often fail to provide the public good in the simultaneous game, and the sequential game successfully eliminates these undesirable outcomes. Sequential giving increases both the likelihood of providing the public good and the participant’s average earnings when fixed costs are high. Despite the equilibrium prediction that a similar result should hold for low fixed costs (6), the study finds instead lower contributions in the sequential than in the simultaneous game. The reason is that with low costs, individuals overcome the strategic uncertainty of the simultaneous game by increasing their contributions to secure provision of the public good, thus contributing more than predicted. By facilitating coordination on the positive-provision outcome, sequential giving eliminates the risk of underprovision and decreases contributions to the predicted level; hence when fixed costs are low, contributions fall below those of the simultaneous game. While behavior under low fixed costs differs from that predicted, the study nonetheless confirms the key insight that the sequential game improves provision when the simultaneous game results in coordination failure. While the laboratory study suggests that sequential giving can play a coordinating role, the insensitivity to refunds calls this explanation of the List and Lucking-Reiley data into question. Is it reasonable to argue instead that their result is due to signaling? Past research has repeatedly shown that the cognitive demands required to implement a signaling equilibrium are substantial.53 To determine whether participants nonetheless can use initial contributions to draw inference on the quality of the public good, Potters, Sefton and Vesterlund (2005, 2007) investigate the role of sequential play when the quality of the public good is uncertain. In contrast to Vesterlund (2003) they examine an environment where the lead contribution is only partially revealing. Specifically, they examine a two-person public good game where the individual in each round is given the option of keeping a dollar or giving it to a public good. The return from the public good is equally likely to be 0, 0.75, or 1.5. The efficient outcome is for both players to contribute when the return equals 0.75 or 1.5. Absent information on quality, the expected return from giving is 0.75, and donors should not contribute. With full information, contributions should occur only when the return from the public good

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equals 1.5. Hence with symmetric information, contributions fall below the efficient outcome. The role of sequential play can be seen in the asymmetric-information case when the quality of the public good is known by one player but not the other. With simultaneous play, the informed player will give only when the return equals 1.5, and the uninformed player will never give. With sequential play, the efficient outcome is achieved, however, when the informed player contributes first. Specifically, the informed first mover contributes for any positive return to the public good (0.75 or 1.5), and the uninformed second mover mimics the action of the first mover because a lead contribution indicates a positive expected return from giving. To investigate the role of signaling, Potters, Sefton, and Vesterlund (2007) examine a 2 × 2 design, varying whether the game is simultaneous or sequential and whether only one or both players are informed of the return from the public good. A round of the experiment proceeds as follows. Participants are randomly paired in groups of two at the beginning of each round, and first movers are informed of the return from the public good.54 First movers then decide whether to invest in the public good. When all first movers have chosen, second movers are either informed of the return from the public good (full information) or told that each of the three values are equally likely (asymmetric information). Similarly the second mover is either informed of the leader’s choice (sequential) or not informed (simultaneous). The second mover then decides whether to invest in the public good. With giving in the sequential game being 50% larger than in the simultaneous game, the experimental results are consistent with the predicted comparative static. Figure 2.5, panel a, shows behavior by the informed leader and uninformed follower in the two asymmetric-information treatments. The sequence of moves is sequential in both the sequential and the simultaneous game; however, only in the sequential game does the follower see the leader’s contribution prior to contributing. Under simultaneous play the follower contributes about a third of the time, and the leader contributes only when it is payoff maximizing for him or her to do so (i.e., when the return is 1.5). By contrast, under sequential play the follower copies the informed leader’s decision by giving 81% of the time when a leader gives and giving only 8% of the time when a leader does not give. Perhaps anticipating the follower’s response, the leader contributes when it is collectively optimal to do so, thus securing that the uninformed follower more frequently contributes when the return is 0.75 or 1.5. As evidence of the efficiency gain, sequential play increases giving by both the leader and the follower when the return is 0.75. While this behavior is consistent with the follower inferring the quality of the public good from the leader, it is also consistent with followers being reciprocal and leaders anticipating this. The two full-information treatments help distinguish between these two hypotheses. Contributions under full information are shown in Figure 2.5, panel b, and suggest that nonpecuniary factors such as reciprocity do not explain the result. When there is full information, contributions are slightly lower (7%) in the sequential than in the simultaneous game. In particular, sequential play does not facilitate greater contributions in the m = 0.75 case. As sequential play does not increase contributions in the full-information case but does increase them in the asymmetricinformation case, the study concludes that signaling is a likely explanation for the increase in giving. Komai, Grossman, and Deters (2011) examine a three-person environment similar to that of Potters, Sefton, and Vesterlund (2005, 2007) and confirm the finding that leadership giving facilitates information transmission. They too find that when

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Panel a: Asymmetric information Informed leader

1 0.8

Sequential

0.8

0.6

0.6

0.4

0.4

0.2

0.2

0

m=0

m = 0 75

Uninformed follower

1

m = 1.5

0

Simultaneous

m=0

m = 0.75

m = 1.5

Panel b: Full information

0.8

Informed follower

Informed leader

1

1

Sequential

0.8

0.6

0.6

0.4

0.4

0.2

0.2

0

m=0

m = 0 75

m = 1.5

0

Simultaneous

m=0

m = 0.75

m = 1.5

Figure 2.5: Contribution rates. (a) Asymmetric Information. (b) Full information. Source: Jan Potters, Martin Sefton, and Lise Vesterlund, “Leading-by-Example and Signaling in Voluntary Contribution Games: An Experimental Study,” Economic Theory 33, no. 1 (2007): 169–82, figures 1–4. © Springer-Verlag 2007; with kind permission from Springer Science + Business Media B.V.

the initial contribution is partially revealing, it is possible for contributions under asymmetric information to exceed those under full information. Meidinger and Villeval (2002) examine instead the effect of sequential play when there is a fully separating equilibrium. They also find that sequential play increases giving, but the increase is driven by reciprocity rather than signaling. An explanation for the different results may be that the fully separating equilibrium is more cognitively demanding. Another explanation may be that Meidinger and Villeval examine behavior in a finitely repeated game, where reciprocity can play a greater role than in the random-matching settings of Potters and others and Komai and others. The key insight of these studies is that despite signaling being cognitively demanding, it can secure, independent of otherregarding preferences, larger contributions under sequential play and render it the preferred solicitation strategy. The evidence found in a number of field studies can also be seen as consistent with signaling playing a role in explaining the frequent use of sequential solicitations. Soetevent (2005) conducts an experiment using 30 churches in the Netherlands to determine the effect of sequential giving. For a period of 29 weeks, the familiar collection

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bags were randomly replaced with open collection baskets. For each offering, baskets were assigned with probability 0.5 and bags were assigned otherwise. While donations in the collection bag are anonymous, those in the collection basket are not, because the contribution can be observed by those seated close to the individual contributing. In addition to varying the collection method, the study also examines under what conditions a particular collection method is effective. At each service there were two offerings; the first was used solely for internal purposes, whereas the second often was used to fund external activities or organizations. The results reveal that baskets increased giving only in the second offering and only when the second offering was used to fund external causes. Furthermore, donations to these causes were also more responsive to pulpit suggestions on donation amounts. One interpretation of the results is that there is greater uncertainty about the quality of an external cause; as a result the informational value of a recommendation or someone else’s contribution is greater in this case. Another interpretation is that there is less of an excuse for avoiding the solicitations for external causes. The reason is that support for the church is typically solicited through direct bank deposits; thus for internal causes it may be easier to claim that “you gave at the office.” Finally, it may be that external offerings give better opportunities to signal unselfish behavior, since there is no transparent material benefit to the contributor from giving. Consistent with Ariely, Bracha, and Meier’s (2009) examination of Bénabou and Tirole (2006), the extrinsic motivation reduces the image signal of giving when behavior is visible. Results of a field experiment examining contributions to public radio (Croson and Shang 2008; Shang and Croson 2009) are also consistent with initial contributions serving as a signal on quality, but once again this is not the only possible explanation for the results. Croson and Shang manipulate the information individuals receive when calling to make a donation during an NPR fundraising campaign. Four different treatments are examined; callers are either given no information on the contribution of others or they are informed, “We had another member, they contributed {either $75, $180, or $300}.” They find that callers who were informed of the higher ($300) donation contributed 12% more than those who were given no information.55 Interestingly, the information affects only the contributions of new donors, whereas it has no effect on renewing members. Examining contributions a year after the campaign, they find that new donors who received information are more likely to give and conditional on giving, they give more. While the differential response to information is consistent with new members being more uncertain about the effect a contribution will have on the station, it may also result from new members being more sensitive to information that suggests a contribution norm. The latter interpretation is also consistent with the results of Martin and Randal (2008). They conduct a field experiment manipulating the monetary content of a glass donation box at an art museum. Similar to List and Lucking-Reiley (2002), this study is by nature solely on sequential giving. Compared to a control of an empty donation box, they find that the contribution frequency increases when the box instead contains coins. Looking at two treatments where the coins are replaced with either large or small bills of the corresponding value, they find a significant increase in mean contributions; the donation propensity, however, drops relative to that for coins. While the three treatments dominate the control, the small-bill treatment secures the largest total donation. Across treatments they note that the composition of the donations (coinage vs. bills) mirrors the composition of the initial content. Evidence that individuals increase their giving in response to large gifts by others is also shown by Frey and Meier (2004) in a study on giving at the University of Zurich. When paying their tuition bill, students were given the option of contributing

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to two social funds where the monetary donation to each of the funds is prespecified (CHF 5 and 7, respectively). Frey and Meier examine the effect of informing students that the share of students who in the past contributed to both funds equaled 64% in one treatment and 46% in another treatment. Controlling for past donations, they find that students give more when they are informed that 64% rather than 46% of potential donors made large contributions in the past.56 Kessler (2015) shows that even a signal of support can affect behavior. In a large-scale field experiment involving more than 36,000 employees at 278 workplaces, he examines the effect on donations of allowing employees to wear a pin indicating support for a charity. He finds that the access to support pins increases average workplace giving by almost 10%. To investigate the channel through which contributions increase, he conducts a complementary laboratory experiment that demonstrates that donations to a charity increase from those exposed to signals of support for the charity.57 As noted, the evidence from the field is consistent with several of the theories on sequential giving. Indeed, the observed response to sequential giving may result simply from individuals having other-regarding preferences or being sensitive to the norms for giving. As shown by Romano and Yildirim (2001), sequential play will be attractive when for one reason or another the best-response functions of followers are positively sloped and sufficiently steep to warrant the first mover to increase her contribution in the sequential game. While laboratory studies suggest that individuals are not solely concerned about the payoff received from the public and private goods, it is less clear that preferences alone can explain the reliance on sequential play.58 Moving beyond Varian’s stark quasi-linear example, researchers have examined the effect of sequential play in the linear VCM, where such other-regarding preferences may be more important. The results from these studies are mixed. Gächter and Renner (2003), Potters, Sefton, and Vesterlund (2007), and Rivas and Sutter (2008) find that contributions are positively correlated, but they do not find that sequential play increases giving. By contrast Güth and others (2007) find that sequential play results in a large and significant increase in giving.59 Examining an environment with heterogeneous endowments, Levati, Sutter, and van der Heijden (2007) find that sequential play increases giving when the distribution of incomes is known.60 Examining an environment with an interior Nash equilibrium, Pogrebna and others (2009) also find that sequential play increases contributions. Finally, Moxnes and van der Heijden (2003) examine a public bad environment and find in a within-subject analysis that investments in the public bad are lower when the decision of one player (the leader) is observed prior to the remainder of the group making a decision. While the effect is small, it is significant. In contrast to the anonymous laboratory setting, in the field it is common that at least the identity of the lead donor is known. This difference may help explain why laboratory studies do not systematically find larger donations in the sequential game. It may be argued that the laboratory is stripped of many of the features that make sequential giving preferable in the field. For example, a central characteristic missing from the laboratory studies is that of the lead donor himself or herself. A better understanding of what may give rise to the behavior suggested by Romano and Yildirim (2001) is achieved by examining whether the typical characteristics of the lead donor are likely to influence behavior in the sequential game. For example, lead contributors distinguish themselves by being wealthy, well known, and respected. These are all characteristics that make the donor ideally suited for signaling the quality of the public good; however, they are also characteristics that may increase giving

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by followers who are concerned about their relative ranking in society.61 Kumru and Vesterlund (2010) show that sequential giving dominates simultaneous giving when donors prefer to associate with those of higher social ranking than themselves. Using a simple linear example, they demonstrate that aggregate contributions and earnings can increase when high-status donors are solicited before rather than after those of low status. To investigate this comparative static experimentally, they induce a status differential in the laboratory using the procedures by Ball and Eckel (1998) and Ball and others (2001). Having completed a brief quiz, participants are assigned to a star or a no-star group, and members of the star group are publicly recognized and given a round of applause. Participants are then reseated in a star or no-star section to the laboratory. They play twelve rounds of a two-person sequential contribution game, where in each round they decide whether to keep a token or place it in a public account with an MPCR of 0.75. Using random matching, in each round participants are paired in a twoperson group consisting of a star and a no-star participant. The between-subject design simply alters whether the star participant contributes before rather than after the nostar participant. They find that low-status followers are likely to mimic contributions by high-status leaders, and this in turn encourages high-status leaders to contribute.62 Total contributions almost double when individuals of high status contribute before rather than after those of low status, increasing from 0.46 to 0.83 tokens. An interesting aspect of the models on sequential giving is that they often predict that both the fundraiser and the donors themselves will have a preference for sequential giving. Examining the Potters, Sefton, and Vesterlund (2007) signaling model, Potters, Sefton, and Vesterlund (2005) show that sequential moves indeed arise endogenously.63 Eighty-one percent of donors agree to move in sequence, and the resulting contributions are larger than those of the simultaneous-move game. In fact, the increase in giving between the sequential and simultaneous game is much larger when sequential play arises endogenously. When sequential play is imposed, the overall increase in giving is around 50%. In contrast, endogenously selected sequential play generates contributions that are 150% larger than those seen when participants instead opt to contribute simultaneously. This effect is primarily driven by contributions in the endogenously arising simultaneous game being particularly small. The finding that the gain from sequential play is greater when it arises endogenously suggests that the advantage of sequential solicitations may be underestimated when we exogenously impose the structure in the laboratory. Arbak and Villeval (2013) also examine endogenous leadership. In a three-person VCM game, participants can contribute either in a first or second round.64 When selecting to contribute in the first round, participants must specify how much they would like to give as a leader. The game is designed such that only one person can be the leader, with the leader being randomly determined. The design secures that leader and follower contributions are identified for those who volunteer to be leaders and helps determine what motivates people to lead. Although it is costly to be a leader, a quarter of participants volunteer to lead, securing that about half the groups contribute sequentially.65 Contributions in these sequential groups are significantly larger than in groups that do not have a leader. Those who volunteer to lead tend to give more and while their contributions decrease slightly when they are instead randomly assigned to be followers, their contributions remain larger than those seen for volunteer followers. Güth and others (2007) also investigate endogenous leadership in a linear VCM, finding that only a third of their groups opt to have a leader, despite groups with a leader being substantially more efficient. The advantage of endogenous leadership is also

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documented in Rivas and Sutter (2011). Examining the VCM they find that exogenous leadership does not increase giving, whereas endogenous leadership increases giving and sustains it over the course of the experiment.66 The experimental evidence on endogenous sequencing suggests that sequential moves may be a particularly robust mechanism when donors benefit from it. 3.1.2 DYNAMIC GIVING Closely related to the research on leadership giving is a literature on giving in a more complex set of dynamic games. Typically, the contribution games are such that donors have many opportunities to give and they are free to contribute whenever and as often as they wish. Importantly donors are informed of the current level of contributions throughout the campaign. Thus donors can slowly increase their contribution and can condition it on the donations by others. As argued by Schelling (1960), this dynamic structure may make it possible for individuals to slowly build trust and ultimately coordinate on a high-provision outcome.67 A number of studies have investigated these dynamic provision environments experimentally. As in the literature on sequential giving, the question of interest has been whether contributions in these dynamic games exceed those in the comparable static game. An early experiment on real-time contributions to public goods is presented by Dorsey (1992). He provides participants matched in groups of 4 with 3 minutes during which they can revise an initial contribution to a public good. Updates on the current provision of the public good are provided throughout the period. A series of different payoff structures are considered.68 Examining the linear VCM with an MPCR of 0.3, where participants can continuously revise their initial contribution upward, he finds a limited effect of continuous-time revisions. In the first 3-minute game, individuals contribute slightly more than 40% of their endowment; however, contributions decrease as the game is repeated and ultimately fall to between 10% and 15% toward the end of 10 games. While the study does not report on contributions in the corresponding static game, Isaac and Walker (1988) examine contributions in the static version of the game and show initial contribution rates of around 35%, declining to about 5% after 10 periods of play. Thus Dorsey’s study does not demonstrate a substantial effect of real-time revisions in the linear VCM.69 Examining a similar 5-person linear VCM with an MPCR of 0.33, Kurzban and others (2001) find that real-time upward revisions facilitate cooperation. Contribution rates of 50% of endowments are sustained over the course of 10 repetitions of the game, thus defying the common trend of decreasing contributions in repeated play of the public good game.70 Contributions are also sustained in Kurzban and Houser’s (2001) examination of dynamic contributions in a linear VCM.71 Outside of the argument that dynamic play establishes trust, there are several explanations for why dynamic contributions may result in greater giving to the public good. Marx and Matthews (2000) demonstrate that there are circumstances where dynamic play is needed to secure positive provision equilibria. When payoffs are increasing up to a completion point and a discrete benefit is secured upon completion, then it may be possible to secure provision only in the dynamic game.72 Specifically, while it is not in the donor’s interest to contribute in the static one-shot game, it is possible to sustain provision in the dynamic game through history-dependent trigger strategies. Duffy, Ochs, and Vesterlund (2007) examine the environment suggested by Marx and Matthews. Specifically, payoffs are such that zero-provision is the unique equilibrium of the one-shot game, whereas positive- and zero-provision equilibria arise in a dynamic

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game where donors can give over several contribution rounds. Of particular interest is whether the completion benefit plays the central role predicted by Marx and Matthews. Dynamic play is predicted to have no effect on giving in the absence of a completion benefit, while it may increase giving in the presence of such a benefit. In building on the theory by Marx and Matthews, the payoff structure of Duffy and others differs from that of Kurzban and others (2001) and Kurzban and Houser (2001), yet the results confirm their finding that dynamic play increases giving. In contrast to the equilibrium prediction, the increase in giving from dynamic play is, however, not sensitive to the presence of a completion benefit. To investigate what causes the increase in giving, Duffy and others conduct an additional treatment where participants can contribute in multiple rounds of simultaneous giving but are not given feedback on contributions between rounds. This new “dynamic” treatment is informationally equivalent to that of the one-shot static game. Casting doubt on the possibility that the increase from dynamic play can be attributed to increased possibilities of building trust, they find that total provision is independent of participants receiving feedback in the dynamic game. This suggests that part of the increase does not result from the ability to condition on contributions by others, and they conclude that special consideration should be given to trembles when comparing static and dynamic games.73 Choi, Gale, and Kariv (2008) examine dynamic contributions in a pure threshold environment, where the return from the public good is fixed and achieved only if contributions are sufficient to cover a fixed cost. While there exist both positive- and zero-provision equilibria in the static version of this game, with sufficiently many contribution rounds, the zero-provision equilibrium is eliminated in the dynamic game.74 Consistent with past studies, they find significantly greater giving when there are multiple simultaneous contribution rounds rather than one. Furthermore, behavior in the dynamic game is shown to be consistent with that predicted by symmetric Markov perfect equilibrium. While they do not examine a no-feedback dynamic treatment, as in Duffy and others, they note that holding the time horizon fixed, behavior responds to treatment variables in a manner predicted by theory, and they conclude that “something other than pure trembling is needed to explain the high provision rates.” The examined studies demonstrate that there is ample reason for fundraisers not to rely on a simultaneous-solicitation strategy. In contrast to the significant work that has been done to uncover the benefits of seed donations or sequential giving, the research on dynamic contributions is more limited, and more research is needed to fully understand why contributions increase in these more complex environments. While the increase in giving may not result solely from mistakes, it is nonetheless essential that scholars properly account for the increased likelihood of error that arises when individuals are given multiple opportunities to give. 3.2 Lotteries Lotteries are another common fundraising mechanism. Although lotteries are not be the ideal source of revenue for governments, research suggests that they may be well suited for nonprofits.75 At first glance it is not clear why nonprofits would prefer to use lotteries over voluntary giving. How can it be to the organization’s advantage that it spends part of its revenue to pay winners of the lottery? Morgan (2000) provides a very intuitive answer to this question. He examines a fixed-prize lottery where the chance of winning is given by the number of tickets the individual purchased relative to the sum of tickets purchased. Assuming that the lottery revenue net of the prize is

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used to finance the public good and that individuals are risk neutral and have quasilinear preferences, he shows that the provision of the public good is larger under the lottery than under voluntary giving. The reason is that the lottery introduces a negative externality, which counteracts the positive externality that results from public good provision. In purchasing an additional ticket, the individual decreases the chances that a given lottery ticket will win. Morgan demonstrates that the individual’s failure to account for this negative externality counteracts the underprovision that results from failure to account for the positive externality associated with increasing provision of the public good. The net result is that funds raised through the lottery cover the cost of the prize and increase provision of the public good. Conducting a laboratory experiment, Morgan and Sefton (2000) compare provision in a VCM and in a lottery. The public good technology is independent of treatment, and money given to the public good secures an MPCR of 0.75. To eliminate the possibility that contributions fall short of the prize, the experimenters fund an 8-token prize; hence funds spent on lottery tickets are directly contributed to the public good. To make the VCM treatment comparable, they treat the 8-token prize as a donation to the public good; with an MPCR of 0.75, each participant in the VCM is therefore given a 6-token bonus payment. The experimental sessions were conducted both at Penn State and at Iowa. I discuss the Iowa design as it is directly comparable to the standard VCM.76 Each session consisted of 20 rounds, 5 of which were for practice. In each round participants were randomly matched in groups of 4, given an endowment of 20 tokens, and asked to contribute to a public good. In the lottery treatment, a 1-token contribution to the public good provided the individual with a ticket to the lottery. While zero provision is the equilibrium prediction in the VCM, the unique Nash equilibrium in the lottery is for each individual to bet 6 tokens. Behavior in the VCM and lottery (lot) treatments are shown in Figure 2.6. Contributions in the VCM are initially at about 50% of the endowment and decrease slightly to about 40% at the end of the experiment. This sustained high level of giving is consistent with that seen in previous VCM experiments with a high MPCR (e.g., Isaac and Walker 1988).77 As indicated by contributions in the lottery (lot), there is, surprisingly, little evidence of a treatment difference. The revenue collected in both the VCM and the lottery is greater than predicted, and the public good provision does not differ significantly from that in the lottery treatment. Morgan and Sefton hypothesize that the deviation from the equilibrium is due to the tension between equilibrium play and efficiency. The greater-than-predicted giving under the lottery may result from the equilibrium being far below the efficient contribution of 20 tokens. To address this concern, they consider a lottery (biglot) with a larger prize of wining (16 tokens). This increase in the prize raises the predicted individual bets from 6 tokens (with a prize of 8) to 12 tokens (with a prize of 16). Behavior in the biglot treatment is more in line with the equilibrium prediction. Bets increase relative to the small-prize lottery, and provision of the public good net of the prize exceeds that of the VCM (with a bonus payment of 6). Morgan and Sefton conclude that behavior is consistent with the predicted comparative static when the equilibrium of the lottery is relatively efficient.78 To rule out the possibility that bets are driven by joy of gambling or confusion, they cleverly conduct a treatment where the lottery is not welfare enhancing. The prize in this badlot treatment is 8 tokens, and bets do not generate a public good. In contrast to the joy-of-gambling hypothesis, Figure 2.6 reveals that behavior quickly converges to the equilibrium bet of 2 tokens. Hence participants realize that it is not in their interest to place bets in excess of the expected value of the lottery.79

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Figure 2.6: Average contributions in Iowa treatments. Legends refer to vcm as the voluntary contribution mechanism with MPCR = 0.75, lot and biglot refer to fixed-prize lotteries with prizes of respectively 8 and 16 where proceeds are given to a public good with an MPCR = 0.75; badlot refers to a fixed-prize lottery where bets are confiscated. Source: John Morgan and Martin Sefton, “Funding Public Goods with Lotteries: Experimental Evidence,” Review of Economic Studies 67, no. 4 (2000): 785–810, by permission of Oxford University Press.

Dale (2004) also compares contributions in a VCM and a lottery. The design is that of Morgan and Sefton (2000), with the exception that Dale increases the prize to 20 tokens and alters the manner in which the prize is funded.80 Mirroring lottery prizes in the field, Dale opts to have the cost of the prize paid out of the bets collected for the lottery and to have the sum of bets minus the prize contributed to the public good. Participants are informed that the lottery is carried out only in the event that the sum of bets equals 19 tokens or more. The equilibrium prediction is for each individual to bid 15 tokens per round. The behavior in Dale’s VCM is similar to that of Morgan and Sefton: individuals initially contribute 10 out of their 20-token endowment, with contributions decreasing to about 8 at the end of the experiment. With mean individual lottery bets falling slightly below 13, the cost of the 20-token prize implies that the resulting provision of the public good does not differ by treatment. In contrast to Morgan and Sefton (2000), Dale (2004) does not find that lotteries improve provision over that of the VCM. Orzen (2008) also investigates the advantage of the lottery. Examining groups of four with an MPCR = 0.5 and a prize of a 100 tokens, he directly funds the prize as in Morgan and Sefton. To secure comparability across treatments, each participant in the VCM is given a 50-token bonus. Although bets are greater in the lottery than in the VCM, it is not until the very end of the 25-round experiment that the lottery secures larger provision. Over the course of the experiment, revenue from the lottery net of the 100token prize falls short of that seen in the VCM. Lange, List, and Price (2007) find the reverse result in a low-MPCR environment. Using an MPCR of 0.3, the tension between equilibrium and efficiency is much reduced, and as in previous studies (e.g., Isaac and Walker 1988) they find that VCM contributions decrease to less than 10% of the individual endowments.81 Confirming the predicted comparative static, the provision of the public good is shown to be greater under the single-prize lottery than under the VCM.

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Laboratory studies typically find that contributions in the VCM fall short of the sum of bets in the lottery. What is unclear is whether the difference between the two is sufficient to cover the cost of the lottery prize. The advantage of the lottery depends on the precise parameters examined. Morgan and Sefton (2000) find increased provision under the lottery when the lottery prize is large, and Lange and others (2007) replicate this when the MPCR is low; however the lottery does not increase provision in the smallprize lottery by Morgan and Sefton (2000) or in the studies by Dale (2004) and Orzen (2008). Landry and others (2006) ask how the lottery fares in the field. Conducting a doorto-door fundraiser for the Center for Natural Hazards Mitigation Research at East Carolina University, they compare contributions in a standard voluntary-contribution environment to one where individuals can win a fixed prize of $1,000. Participants were informed that their chances of winning depend on their ticket purchases relative to the number of tickets purchased by other households in the county. More than 2,000 households were approached for either the standard donation treatment or for the $1,000 lottery treatment. Households that were home when approached were twice as likely to contribute under the lottery treatment. The gross proceeds in the lottery treatments were roughly 50% larger than that of voluntary giving, with the response primarily resulting from a greater participation rate under the lottery. Similar to the laboratory studies, the resulting provision is not larger. When faced with a $1,000 prize, collections netted $688, thus falling $312 short of the prize. By comparison, $452 was raised through voluntary contributions. Landry and others note that the provision under the lottery would be larger if more households had been approached. Assuming that mean bets remain the same, they show that the public good provision under the lottery would surpass that under voluntary contribution provided that 6,000 households were solicited. In evaluating the revenue of the lottery to that of voluntary giving, it is important to keep in mind that the lottery comes with the risk that bets can fall short of the prize. As an alternative, it may therefore be tempting to consider a revenue-dependent and “safe” lottery, where a fixed share of the revenue is used for the prize and the remainder is used for the public good. For example, the revenue may be split equally between the prize and contributions to the public good. Unfortunately, as shown by Morgan (2000), the revenue-dependent, or pari-mutuel, lottery is unlikely to be a successful fundraising mechanism. The reason is that in the revenue-dependent lottery, the purchase of an additional lottery ticket does not impose a negative externality on others. While an additional ticket decreases the probability that any given ticket will win, it simultaneously increases the prize that can be won on a given ticket. If the size of the prize is a linear function of the revenue, then these two effects cancel each other out. Thus the purchase of an additional lottery ticket does not impose a negative externality on others and the public good provision that results under a revenue-dependent lottery is precisely that of voluntary provision. Along with his investigation of the VCM and the fixed-prize lottery, Dale (2004) also examines the revenue-dependent lottery. He finds that mean contributions in both the VCM and revenue-dependent treatment are greater than predicted but that contributions and bets were similar in the two treatments. Accounting for the payment of the lottery prize, provision is therefore lower in the revenue-dependent lottery. Another variation on the fixed-prize lottery that has received some attention is the consideration of multiple rather than a single lottery prize. Lange, List, and Price (2007) examine the effect of multiple lottery prizes under the assumption that each individual can win only one prize. The restriction of one prize per individual implies that the

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predicted revenue when faced with homogenous and risk-neutral individuals is greater with one rather than multiple prizes. However, when the population is sufficiently risk averse or when the marginal value of the public good differs sufficiently across individuals, then there may be benefits to splitting a fixed prize into multiple small prizes of the same aggregate value. Experimental examinations of the multiple-prize lottery do not show that it is superior to the single-prize lottery. Lange and others conduct a laboratory experiment with groups of four varying the MPCRs such that one person has an MPCR of 0.9 and the remaining three an MPCR of 0.1. They find, contrary to the equilibrium prediction, that public good provision is greater with a single prize of 80 than with three prizes of 50, 20, and 10. A field experiment by Landry and others (2006) also fails to find a difference between having a lottery with a single prize rather than multiple prizes. In fact, their results show that revenue is the same whether participants are informed that they may win $1,000 or one of four $250 prizes. 3.3 Auctions Morgan’s recognition of the negative externalities associated with charitable lotteries has given rise to a broader literature on competitive fundraising.82 A central question is whether such mechanisms in general improve provision of public goods. Of particular interest have been the commonly observed charity auctions. Winner-pay auctions are frequently used to raise funds for a public good, and social fundraising events are often combined with either a silent auction or a standard oral ascending auction. Will these winner-pay auctions also increase provision? As in the lottery, an increased bid imposes both a positive and negative externality on others, the first resulting from the increased provision of the public good and the second from the decreased likelihood that others have the highest bid and will win the item. In contrast to the lottery, the winnerpay auction uses only the winner’s bid to provide the public good; thus by winning the bid, the individual eliminates the contribution by others. This latter effect is often detrimental when comparing it to the lottery. On one hand, the winner-pay auction allocates the auctioned item to the highest bidder, thus improving on the stochastic allocation rule of the lottery. On the other hand, the winning bid by one individual eliminates the bids and public good contributions by others. By contrast, both winning and nonwinning ticket holders contribute to the public good in the lottery.83 Goeree and others (2005) and Engers and McManus (2007) provide theoretical examinations of the revenue from various types of charity auctions as well as from lotteries.84 Examining a private value and incomplete-information environment, it is shown first that adding a charity component to an auction increases the winning bid. Second, the standard revenue-equivalence result is broken in the charity auction because the second-price auction dominates the first-price auction.85 The reason is that bidders who don’t win the auction benefit from a higher winning bid and therefore have an incentive to drive up the price in the second-price auction. Third, and more importantly, neither of these winner-pay auctions is optimal. Goeree and others and Engers and McManus show that all-pay auctions dominate both winner-pay auctions and lotteries. The reason is that all-pay auctions both secure that the item is allocated to the bidder with the highest valuation and that by bidding, an individual does not have to forgo the positive externality that results from the bids of others. Much experimental work has been done to shed light on behavior in charity auctions. An initial question of interest is whether the revenue from a charity auction is greater than that from a noncharity auction. That is, does the winning bid increase when a

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share of the revenue is given to a public good? To get a sense of bidding in charity auctions, Isaac and Schnier (2005) look at bids in three nonexperimental fundraising auctions. The number of items for sale in each of the auctions ranges between 135 and 194 items. Only in one auction do they see bids in excess of the item’s assessment.86 However bidding below assesment cannot be interpreted as bidders ignoring the charity component of the auction or as evidence that the auction was unsuccesful. The relevant question is how the revenue from a charity auction ranks relative to that of a comparable noncharity auction.87 Salmon and Isaac (2006) show that if the donor’s benefit from the public good is independent of who provides the good, then we should not be surprised to see essentially the same revenue in the two auctions. Under this pure altruism assumption, it would require a very strong preference for the public good to secure a noticeable response in the revenue from the charity auction. The reason is that the benefit from the public good increases both the return and cost of raising one’s bid, and these counterbalancing incentives theoretically net out. The incentive to bid to secure provision of the public good is outweighed by the fact that a raised bid eliminates another person’s bid and, thus, that person’s contribution to the public good. The revenue in the winner-pay auction is found to be insensitive to the return from the public good. Isaac, Pevnitskaya, and Salmon (2010) examine this hypothesis experimentally in a private-value auction with incomplete information. In a case where the auction’s revenue is used to fund a public good, they see only moderate revenue increases in response to increases in the MPCR. Furthermore, they see no or limited evidence of more aggressive bidding when proceeds are given to an actual charity, and this result does not change when soliciting bids from individuals who are committed to the nonprofit. Similarly, Schram and Onderstal (2009) find that the revenue from a firstprice auction is the same whether the MPCR is 0 or 0.5. The limited evidence that bids are influenced by who receives the proceeds led Isaac and Schnier (2005) to conclude that for charity auctions, the main aspect of charitable giving is from those donating items to the charity auction, the bids themselves seem insensitive to the allocation of the auction’s proceeds. Similarly, Orzen (2008) concludes that winner-pay charity auctions should not be seen as securing charitable contributions but rather as a simple way of converting donated items into cash.88 The works by Goeree and others (2005) and Engers and McManus (2007) suggest that there are more successful ways of converting such items into cash. In particular, the public good provision is predicted to be greater when using an all-pay auction than a winner-pay auction. In fact, the all-pay auction is predicted to outperform a series of fundraising mechanisms. Experimental studies have examined the potential advantage of the all-pay auction, asking whether the all-pay auction is superior to the VCM, the lottery, and/or the winner-pay auction. Orzen (2008) compares the VCM, the lottery, and all-pay auctions in a commonvalue and complete information environment. He considers two different types of allpay auctions: one where all bidders pay their bid and another where bidders pay the minimum bid. Goeree and others showed that this later all-pay auction dominates the first. The reason is that the lowest bidder will recognize that an increase in his or her bid increases the payment of all others. The experiment consisted of 25 rounds, participants were randomly matched in groups of 4 at the beginning of each round, and each was given an endowment of 100 tokens, which—depending on treatment— could be bid in the auction, bet in the lottery, or placed in a public account with a 0.5 MPCR. To secure nonnegative public good provision, the prize was provided by the experimenter and participants in the noncompetitive mechanisms were given an

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individual bonus payment of 50 tokens. Initial behavior does not respond to treatment but then separates. As predicted, the revenue of the VCM is dominated by that of all other treatments. The revenue from the lottery and the pay-your-bid all-pay auction are the same. The pay-minimum-bid all-pay auction dominates all the examined mechanisms and ultimately becomes efficient at the end of the experiment. Accounting for the cost of the lottery prize, the pay-minimum-bid all-pay auction dominates the VCM. Schram and Onderstal (2009) examine the all-pay auction in a private value and incomplete information setting. They examine three mechanisms: a lottery, a winnerpay auction, and a pay-your-bid all-pay auction. All mechanisms are considered with and without a public good component. While the examination of mechanisms is between subjects, each participant sees the mechanism both without and with a public good component (MPCR = 0 vs. 0.5). Participants made decisions over 28 rounds and were randomly matched in groups of 3 people at the beginning of each round.89 The revenue of the all-pay auction is found to exceed that of the lottery, and in contrast to the equilibrium prediction the lottery exceeds that of the winner-pay auction.90 The results of the study lead Schram and Onderstal to provocatively argue that if the charity responsible for selling Eric Clapton’s legendary 1956 Fender Stratocaster “Brownie” had used an all-pay auction rather than a winner-pay auction, then they could have raised the price of $497,500 by at least $100,000. Similar to Orzen (2008), Corazzini, Faravelli, and Stanca (2010) examine an environment with a common value prize; however, in contrast to earlier studies they let endowments be randomly determined and unknown to the other members of the group. Three mechanisms are examined: pay-your-bid all-pay auction, lottery, and VCM. While the all-pay auction is predicted to dominate the lottery slightly, the two raise the same revenue at the beginning and at the end of the experiment. The lottery, however, dominates in the intermediate rounds. Accounting for the prize, the VCM raises essentially the same revenue as the all-pay auction. The reported results show mixed evidence on the attraction of the all-pay auction over the lottery. While Orzen finds no revenue difference between the lottery and the pay-your-own-bid all-pay auction, Schram and Onderstal find that the all-pay auction dominates the lottery, and Corazzini and others find the opposite ordering. In an attempt to better understand the merits of the all-pay auction, researchers have also begun to investigate this mechanism in the field. Carpenter, Holmes, and Matthews (2008) compare three sealed-bid auctions in a field experiment. In addition to examining a first-price auction and a first-price all-pay auction, they also examine a second-price auction. Each of these auctions was used at a fundraiser for a preschool. Inclement weather on the date of the all-pay auction caused them to repeat the all-pay auction at a different preschool. While the revenue of the all-pay auction is predicted to be greatest, the revenue from the first-price winner-pay auction is predicted to be smallest. The results of the field experiment reveal the opposite ordering, with the revenue from the all-pay auction being the lowest and that of the first-price auction being the highest. The primary reason for the reversed ordering is that the participation rates differ markedly between the mechanisms. The participation rate was 53% in the firstprice winner-pay auction, 39% in the second-price winner-pay auction, and, finally, a mere 13% and 14% in the two all-pay auctions. Based on surveys of the participants, they conclude that the different participation rates may result from the participation costs of the auctions being perceived differently. Indeed a survey reveals that the all-pay auction is perceived as less fair and significantly more difficult to understand.

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Onderstal, Schram, and Soetevent (2013) find similar results in a large door-todoor fundraising experiment; 4,500 households were approached and presented with one of four treatments: an all-pay auction, a lottery, a nonanonymous solicitation, or an anonymous solicitation. Despite improving the Carpenter, Holmes, and Matthews’ (2008) description of the all-pay auction, they find that households are least likely to contribute under this mechanism, and the revenue in the all-pay auction is found to be lower than in any of the other mechanisms.91 The low contribution rate is attributed in part to the all-pay auction crowding out the intrinsic motive for giving and in part to donors being reluctant to make a nonanonymous contribution. Interestingly, the results reveal that conditional on donating, households contribute less when asked to report their name along with the donation than under the anonymous solicitation, where they could just contribute money. While the lottery is shown to outperform the other nonanonymous mechanisms, the anonymous solicitation raises the largest number of funds. The authors conclude that in relying on voluntary and anonymous contributions, fundraisers must have been relying on the correct mechanism all along. The theoretical literature on competitive fundraising mechanisms suggests that both lotteries and all-pay auctions are superior mechanisms. While some experimental studies have confirmed this for lotteries, the field evidence on all-pay auctions is far less promising. 3.4 Rebates and Matches Perhaps the most direct way of enticing individuals to give is to change their cost of making a donation. The cost of making a contribution to nonprofits may be altered either by offering matching funds to a donation (be it from an employer or another donor) or by offering that part of the donation be refunded (in the form of say a tax deduction). Past work on the sensitivity of charitable giving to the price of giving has used nonexperimental data, such as tax filings or survey data, to determine how donations respond to changes in the marginal tax rate, and thereby to changes in the marginal cost of giving. It is not until recently that researchers have begun to use experimental techniques to determine the price sensitivity of charitable giving. The results on the price sensitivity of giving help determine whether and how a nonprofit benefits from converting a contribution into a match, and it addresses a recent literature advocating that individuals would give more if the tax-deduction benefits were more salient and if it were less cumbersome to file for such deductions.92 This observation led Thaler and Sunstein (2008) to propose the introduction of a charity debit card, which keeps track of all charitable donations and informs the donor of the net cost of such contributions. The extent to which such an initiative would increase giving, however, relies on how donors respond to salient changes in the price of giving. Experimental work helps address this issue by informing participants directly about the cost of giving. In reviewing the experimental literature on the price sensitivity of giving, I will focus on studies that examine how responsive giving is to matches and rebates. Karlan and List (2007) conduct a field experiment to examine how contributions respond to different match rates. Solicitations were mailed to 50,000 supporters of a “liberal politically- oriented non-profit that focuses on social issues and civil liberties.” All potential donors were presented with the same request for funds, but the incentives for giving varied across treatments. Four different relative prices of giving were examined: no match (control), a $1 for $1 match, a $2 for $1 match, and a $3 for

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$1 match. Comparing the three match treatments to the control reveals that the match increased both the likelihood of contributing (by 22%) and the amount given (by 19%); thus total contributions to the nonprofit increase when a match is offered. In contrast to expectations, they find, however, that the response to the match is not sensitive to the size of the match.93 Increasing the preceding match, the one-for-one level does not affect contributions. Karlan and List note that this insensitivity to magnitude is similar to the scaling effect documented by Kahneman and Knetsch (1992). Interestingly, the response to the match is seen in only some geographical areas. Specifically, the effect of a match is driven entirely by the response in “red” states (states where Bush won the 2004 presidential election). There is little or no effect of the match in “blue” states. This heterogeneity suggests that changes in the match are not simply viewed as a change in the price of giving. A follow-up study by Karlan and others (2011) conducts a field experiment to examine the effect of smaller matches. While using a different organization, they continue to examine donations to a liberal organization that focuses on civil justice issues: 20,000 supporters received a solicitation with either no match (control), a $1 for $1 match, or a $1 for $3 match. While the results confirm the previously documented insensitivity to the match level, relative to the control treatment they do not find that a match has any effect on giving. That is, contributions on average do not respond to the price of giving. As in their earlier study, they find that the lack of an effect masks a heterogeneous response by donors. While donors who are actively supporting the organization respond positively to the match, lapsed donors either don’t respond or decrease their contribution in response to the match. Limited evidence of an effect of a match is also documented in Rondeau and List (2008). This study examines the effect of matches on the provision of a threshold public good. That is the public good is provided only if sufficient funds are raised. Sierra Club supporters were asked to contribute toward a K–12 environmental education program. Potential donors were informed that donations would be refunded if funds fell short of a prespecified level. Despite examining a different provision environment, they confirm the Karlan and others’ finding that the introduction of a match does not significantly increase contributions.94 From the nonprofit’s perspective, it is not solely a question of determining the immediate consequences of a temporary match. The long-term consequences are equally important. For example, the match may encourage more people to give and thus increase the existing donor base and future contributions, or it may result in an intertemporal substitution causing present giving to increase while future giving decreases, or it may be that a temporary match crowds out the intrinsic motive for giving, potentially causing a permanent reduction in future giving. Meier (2007) conducts a randomized field experiment to examine both the short- and long-run consequences of short-term matching incentives. As in his earlier work, the experiment is conducted at the University of Zurich, where students can contribute to two social funds (with contribution levels of CHF 5 and 7, respectively). Meier examines the effect of introducing one of two temporary matches. Individuals who contribute to both social funds, with a cost of CHF 12, will trigger a donation from an anonymous donor of either CHF 3 or CHF 6, corresponding to a match rate of either 25% or 50%, respectively. The effect of the match is identified by comparing the contributions of the treatment groups to that of a control group, which was not offered a match.95 Meier finds that individuals are more likely to contribute to both funds when doing so triggers a match; however, the response does not differ significantly between the 25%

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and 50% match. The consequences of the temporary match are less positive after the match is removed. Students who were subjected to the match decrease contributions in the three periods after the match is removed. This decrease in giving is so large that it overwhelms the initial positive effect, and the overall effect of the match on the contribution rate is negative. In trying to understand the cause of this detrimental effect, Meier examines the effect the match has on donations by those who were contributing to both funds prior to the match. He finds that these maximum contributors also decrease their giving after the removal of the match. This latter result causes Meier to argue that the long-run effects of a match do not result merely from intertemporal substitution, but also from the match undermining the individuals’ intrinsic motivation for giving. A similar detrimental effect of extrinsic incentives on intrinsic motives have been demonstrated and discussed by, among others, Frey (1997), Gneezy and Rustichini (2000), Gneezy (2003), and Bénabou and Tirole (2006).96 The evidence from the reported field experiments demonstrates at best a small positive price elasticity of giving. Despite the price of giving being very salient, it does not appear that it has a substantial impact on the individual’s contribution to nonprofits. Accounting for tax deductions, Karlan and List (2007) find a price elasticity of 0.225 between no match and any positive match, and they find a price elasticity of zero conditional on a match. Karlan, List, and Shafir (2011), of course, find no evidence that contributions are sensitive to the presence of a match. By all accounts this effect is low relative to that seen in nonexperimental data; see, for example, Randolph (1995), Auten, Sieg, and Clotfelter (2002), and Bakija and Heim (2011). One possible explanation for these differences may be that the experimental data relies on changes in a match, whereas the nonexperimental analyses rely on the response to changes in tax deduction. Eckel and Grossman (2003) examine whether the behavioral response is the same under equivalent matches and rebates. As an example, they ask whether the gross donations a nonprofit receives under a 100% match differ from those received under a theoretically equivalent 50% rebate. Participants in their laboratory study are presented with a series of different budgets and asked to allocate money between self and a charity of their choice.97 While the simultaneous choice of donation and charity differs from the cases where the incentive to give is offered by a particular organization, it mirrors the environment an employee faces when his or her employer offers to match a contribution or that faced by a taxpayer when charitable contributions are tax deductible. Participants were presented with matches and rebates corresponding to relative prices of $1, $0.80, $0.75, and $0.50.98 The data reveal that donors presented with a match contribute 1.2 to 2 times more than those presented with the equivalent subsidy. This differential response to equivalent matches and rebates has been replicated in a series of laboratory studies (Eckel and Grossman 2006a, 2006b, 2008; Davis, Millner, and Reilly 2005; Davis and Millner 2005; Davis 2006), and while the difference between the rebate and match tends to be smaller in the field than in the laboratory, it still remains substantial and significant (Eckel and Grossman 2008, 2016). Four explanations have been provided for the differential response. Eckel and Grossman (2003) argue that the source of the difference lies in the match and rebate frame. While the rebate is cast in a reward frame, the match is perceived as being in a cooperative frame. Thus the rebate incentive may adversely affect the individual’s intrinsic motive for giving. Davis, Millner, and Reiley (2005) argue instead that the result can be attributed to confusion. Noting that contributions across incentives center around 50% of the endowment, they argue that the differential effect of rebates and matches results from a confusion-based constant pass rule. Davis and Millner (2005)

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propose that part of the effect may be attributed to an aversion to rebates. Finally, Davis (2006) argues that an isolation effect may explain the finding, suggesting that individuals focus only on the variable they have under their control, namely, the amount of money they initially transfer. According to the isolation effect, the donor’s initial contribution, also referred to as the checkbook donation, will be the same for an equivalent match and rebate, which in turn will imply that total contributions under the match exceed those of the rebate by precisely the magnitude of the match. The attempts to tease these explanations apart have been many. The work by Davis and coauthors have centered on demonstrating that the finding is not unique to charitable giving, thus casting doubt on the extent to which it is due to a crowding out of intrinsic motivations. Davis, Millner, and Reilly (2005) show that an even greater difference between the match and rebate is found when individuals instead are making subsidized investment decisions. Similarly, Davis and Millner (2005) replicate the finding when individuals are offered a discount on a candy bar in the form of half-off (rebate) or two for the price of one (match). As for the nonprofit donations, they find that the participant’s expenditure (on chocolate bars) is greater under the match incentive than it is under the rebate incentive. To better understand the role of confusion, Davis, Millner, and Reilly (2005) let donations go to a prespecified charity and present participants with only two decisions at a time, namely, the equivalent match and rebate. They also provide participants with a complete payoff table specifying the equivalent payoff consequences of their decisions for the nonprofit and the individual. While these changes to the experimental design reduce the difference between the match and the rebate, the contributions to the nonprofit continue to be larger under the match. This robustness of the effect suggests that confusion is unlikely to be the only explanation for the observed phenomenon. Based on evidence from a survey, Davis and Millner (2005) argue that the remaining difference results from “rebate” aversion. Such an aversion also helps explain their finding that giving under rebates is lower than when individuals are faced with a straight price reduction. Eckel and Grossman (2006b) have also attempted to simplify the design to secure that the effect cannot be attributed to confusion. They move away from the initial within-subject design and find that the result remains when participants are subjected to only one of the two subsidy forms. In fact, it appears that the difference increases in the between-subject design. To understand the potential role of rebate aversion Eckel and Grossman (2006a) conduct an experiment where prior to making the contribution decision, participants select whether they prefer a one-for-one match or a 50% rebate. Once they have selected their preferred subsidy, they are then asked to make a contribution under the selected incentive. They find that the rebate and match schemes are selected at the same frequency, and they conclude that the evidence is inconsistent with rebate aversion. However, consistent with previous evidence, they continue to find that total contributions to the nonprofit are larger for those who selected the match than for those who selected the rebate. Finally, Lukas, Eckel, and Grossman (2011) acknowledge that the choice set under the rebate is smaller than under the match, and they therefore allow participants to borrow against future rebates such that the set of possible contributions are the same under the two treatments. In addition, they include payoff tables as in Davis, Millner, and Reiley (2005). Once again the differential remains. Davis (2006) does find a setting where total contributions are the same under the match and rebate. Changing the presentation of the two incentives, he finds that the amount the donor initially gives under the rebate exceeds that of the match by precisely the size of the match. In his modified instructions, he informs participants

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under the match that for each dollar of a total contribution to the nonprofit, $0.50 was donated by the donor and $0.50 resulted from the match. Similarly, under the rebate he informs participants that for each dollar of a given contribution to the nonprofit, the $1 came from the donor, who subsequently received a $0.50 rebate. Under this modified presentation he finds that the total contribution to the nonprofit is independent of the form of the subsidy. He sees this as evidence that the initial differences resulted from participants ignoring the effect of the subsidy, and he argues that an isolation effect causes individuals to focus only on the amount they initially give, that is, the checkbook amount.99 Lukas, Eckel, and Grossman (2011) in turn argue that an isolation effect not only implies that the checkbook amount is constant under an equivalent rebate and match, but also that within a given incentive, the checkbook donation is independent of the offered subsidy rate. Expanding the set of offered match and rebate rates, they find first that the checkbook donation is independent of the match rate, thus confirming the findings of the field studies previously discussed. However, in their data the checkbook donation is sensitive to the rebate rate. They conclude that the response to rebate is inconsistent with the isolation effect and note that the differential response to the match and rebate can be seen as participants passing along to the charity the full benefit of the subsidy in the match treatment but less than the full benefit in the rebate treatment.100 In light of nonexperimental field data, the experimental evidence on the insensitivity to the price of giving is surprising, in particular because the experimental data are presenting the response to salient price changes. In contrast to the proposal by Thaler and Sunstein (2008), it may not be possible to improve giving by making the cost of giving more salient. So why would the price sensitivity in the laboratory differ from that derived from actual tax-deductible giving? In explaining the difference, it is important to recognize that the examined changes in the price of giving may not be directly comparable. For example, as the value of a charitable tax deduction improves, we are not only influencing the incentive to make contributions to nonprofits but also the incentive to exaggerate such contributions. In comparing the response to price changes using experimental and nonexperimental data, it is crucial that this incentive to cheat is properly accounted for.101 While the verdict is still out on what causes the response to rebates and matches to differ, it remains clear that matches are more effective in securing contributions to public goods. If a nonprofit were given the choice between offering a rebate or a match, then they should clearly opt for the match. In selecting a match, it is interesting to note that the effect on total contributions arises from the match rather than from the effect the incentive has on donors. Laboratory and field evidence both suggest that the checkbook donation an individual makes is relatively insensitive to the match rate; the observed increase in gross donation results from the match itself. While the emphasis in past work has been on the effect such matches introduce for the donor who is offered a match, it may be argued that the alternative to the match is not necessarily no match, but rather that the donation given as a match is given instead as a direct donation to the nonprofit. Huck and Rasul (2011) present such a study. Using four different treatments, they varied the solicitation letters that were sent to 14,000 attendants at the Bavarian State Opera House. In a control treatment participants were simply asked to give, in two matching treatments participants were informed that a lead donor had offered to match contributions at a rate of 50% or 100% up to a lead contribution of €60,000 and in a leader treatment they were informed that a lead contribution of €60,000 had been made. The latter treatment helps identify the separate effect of having a match. With the average donor contribution in the leader

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treatment being €132, they find that contributions decrease to €101 under the 50% match and to €92.3 under the 100% match. When separating the role of having a lead contribution, they find that the match itself decreases the amount individuals give. They conclude that fundraisers may secure larger contributions by simply announcing a large initial contribution, and abstaining from converting it into individual matches.102 With individual contributions absent the match being only €74.3, the authors note that organizations nonetheless are well advised to accept gifts for which the donor insists on offering a match. Perhaps in fully understanding the precise role of the match and the lead donations it may be of interest to also incorporate the leader’s decision to offer such donations.

4 CONCLUSION The literature on public good experiments has grown substantially since Ledyard’s (1995) handbook chapter. In trying to narrow the review of research since then, I opted to focus on the research on charitable giving. Moving beyond the linear VCM environment, researchers have gained important insights on what motivates people to give and on the mechanisms used to encourage such gifts. In reviewing the literature I focused on mechanisms for which a large number of studies had been conducted. While the discussion centered on one mechanism at a time, many of these studies simultaneously examine multiple mechanisms. The study by Huck and Rasul (2011) demonstrate that added insights may be gained by simultaneously examining different types of mechanisms. By considering both the effect of a lead donation and matching, Huck and Rasul show that the response to a lead donation likely explains why giving is sensitive to the presence of a match but not the level of a match. In limiting the review to a few central topics, many vibrant research questions received no discussion. For instance, researchers continue to improve our understanding of what motivates individuals to give. Particularly exciting is the research on the tendency to give to an identifiable rather than statistical recipient. This “identifiable victims” effect first noted by Schelling (1968) is supported by anecdotal evidence but has also been documented using experimental methods. Small and Loewenstein (2003) show that transfers in a dictator game are larger when a recipient’s ID number is determined before rather than after a donation decision is made. It is, however, not easy to disentangle the identifiable victim effect. Small, Loewenstein, and Slovic (2007) find in a series of field experiments that the attempt to help people recognize the discrepancy in giving toward identifiable and statistical victims has perverse effects as it decreases giving to identifiable victims and does not increase giving to statistical victims.103 They conclude that deliberative thinking causes people to become less sympathetic toward identifiable victims. In reviewing the literature on various fundraising mechanisms, the emphasis was placed on the topics that have been particularly research active; however the variables used to design a fundraising campaign are many, and researchers are beginning to examine many more of the options fundraisers consider when designing a campaign. For example, while much work has been done on threshold provision of public goods, researchers are just now beginning to ask how these thresholds come about. In some cases the threshold for a campaign is determined by nature; however, there are many instances where the threshold is a strategic choice by the fundraiser.104 Dorsey (1992) noted that dynamic provision was very effective when a threshold had to be reached

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to secure provision of the public good, leading him to suggest that a fundraiser may benefit from using an all-or-nothing strategy. Menietti, Morelli, and Vesterlund (2009) show that if a threshold can be strategically selected, then the fundraiser is likely to select too high a threshold, resulting in overprovision of the public good. Indeed, their laboratory study shows that overprovision can be secured by setting an inefficiently high threshold. In examining fundraising mechanisms, researchers have also begun to account for phenomena such as reciprocity and time-inconsistent preferences. For example, Falk (2007) conducts a large-scale field experiment to examine the role gift exchange plays in charitable giving. Sending 10,000 solicitation letters, he varied whether the solicitation contained no gift, a small gift, or a large gift. The small gift was one postcard plus envelope, while the large gift was a set of four postcards with four envelopes. The presence of a gift had a substantial effect on the likelihood that individuals gave, with the small gift increasing the frequency of giving by 17% and the large gift increasing the frequency by 75%. There is also evidence that fundraisers may benefit from acknowledging that donors have time-inconsistent preferences. Frey and Meier (2004) examine the effect of changing the manner in which funds were solicited at the University of Zurich. Before 1998 students would receive two separate invoices, one billing them for their tuition plus their donation and the other just for their tuition, and they chose which invoice to return (i.e., with or without the donation). Starting in 1998 students were instead given one bill and asked to tick off a box to indicate their willingness to contribute. However, they no longer had to pay immediately but could wait a month before they would receive an invoice for their contribution. Interestingly the percentage of contributors increased from 44% to 62% after this change. Similar results are shown by Breman (2011), who conducts a field experiment to explore intertemporal choices in charitable giving by varying the timing of commitment and payment. Her work builds on that of Thaler and Benartzi (2004). The design is as follows: monthly donors were asked to increase their contributions immediately, in one month, or in two months. She finds that the mean increase in donations is significantly higher when donors are asked to precommit to future donations (32% in one month, 11% in two months). Follow-up data show that the treatment effect is persistent, thus making the strategy highly profitable to the charity. An area that deserves increased attention is that of the long-term effects of a campaign. On one hand, the initial incentive to give may simply encourage people to give now rather than later, thus decreasing future contributions. On the other hand, once donors give, it has been shown that they continue to give; hence it may be worthwhile to sacrifice funds in the short term to secure future “warm-list” donors. Landry and others (2010), Shang and Croson (2009), and Meier (2007) are among the few studies that examine the long-term effect of the fundraising initiative. Moving beyond the one-shot solicitation or even the one-organization solicitation is clearly an important avenue for future work. As the literature continues to become more field oriented, we increase the likelihood that the results of our experimental studies will be used to directly inform policy and fundraising designs in the field. This field-oriented move has thus far been carefully founded in economic theory. The strengths of a theoretical foundation are many: it informs us on what factors or parameters are important, how we might identify them, and how we might interpret their behavioral response. Importantly, it also gives us a common reference point and framework that allows researchers who use the same language to engage in a dialog on what drives behavior, thus generating the many

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bodies of work reviewed in this chapter. The increased attention to behavior in the field has helped us gain new and exciting insights on how and why people give to charity. As researchers are collaborating with organizations to shed light on which fundraising techniques are most effective, it is important to be wary of the temptation to consider solicitation modifications that are perhaps best examined by those trained in marketing. If we are to build our knowledge of the market for charitable giving through a directed dialog, then it is essential that our research remains founded in economic theory.

NOTES 1. See, for example, Ostrom, Walker, and Gardner (1992), Fehr and Gächter (2000), Sefton, Shupp, and Walker (2007), Ehrhart and Keser (1999), Page, Putterman, and Unel (2005), Cinyabugum, Page, and Putterman (2005), and Ahn, Isaac, and Salmon (2008, 2009). 2. An indication of the substantial interest in this topic is that Ledyard’s handbook chapter has 3,500 Google citations. 3. For example, examining the classic linear public good game, Zelmer (2003) presents a meta study of the factors that influence cooperation, and Croson (2007, 2008), Gächter and Thöni (2007), and Holt and Laury (2008) review the literature on behavior and motives for giving; finally, Chaudhuri (2011) reviews the effect on giving of conditional cooperation, punishments, communication, and endogenous group formation. The examination of group mechanisms is also closely related to the growing literature on political economy: see Palfrey (Chapter 6). For related reviews of the charitable giving sector, see Andreoni (2008) and List (2011). 4. Contribution maximization may result from a concern for the nonprofit’s output or from a concern for personal employment and professional achievement as a fundraiser. 5. Philosopher Thomas Nagel notes, “by altruism I mean not abject self-sacrifice, but merely a willingness to act in the consideration of the interests of other persons, without the need of ulterior motives” (1970, 79). Dawes and Thaler (1988) argue that altruism is “taking pleasure in other’s pleasure.” 6. A common critique of the dictator game is that the decisions do not mirror those seen outside of the laboratory. It is argued that individuals outside of the laboratory rarely make transfers to random strangers. This argument seems to miss the point that dictator games are meant to capture environments where someone is asked to give a transfer (or a favor) to a random stranger. A positive response to such directed requests are not uncommon in the field, and the critique that the dictator game has no parallel outside of the lab seems exaggerated. 7. Recently economists have also begun to study contributions in nonlinear public good games where the Nash equilibrium and Pareto efficient outcomes are interior to the strategy space. Interior equilibria have traditionally been secured by making the return to either the private or the public good nonlinear. In reviewing the literature Holt and Laury (2008) conclude that neither design results in equilibrium play. However, examining a 2-person and 4-person public good game with piecewise linear returns, Bracha, Menietti, and Vesterlund (2011) and Recalde, Riedl, and Vesterlund (2013) document a very high frequency of equilibrium play. 8. Andreoni (1995) presents an early examination of intentionality. He compares decisions in the linear VCM to those in a comparable game where participants are paid based on relative rather than absolute performance. While the choice set and earnings are comparable in the two games, only confusion can explain giving in the second zero-sum game. While there is evidence of both confusion and intentional giving, Andreoni concludes that about half of the contributions in the linear VCM are made by individuals who understand that free riding is an option but nonetheless opt to contribute (see Anderson, Goeree, and Holt (1998) and Houser and Kurzban (2002) for comments on the ability to draw inference on confusion in this environment). Examining a finitely repeated VCM, Houser and Kurzban (2002) follow an approach similar to Andreoni (1995); however they compare contributions that result when the other members of an individual’s group are human versus when they are computers. Setting the computer contributions at levels comparable to that seen in the human interaction, Houser and Kurzban (2002) conclude that half of the contributions in the finitely repeated VCM can be attributed to confusion (see also Ferraro and Vossler 2010). For further investigations of confusion versus intentional play in the repeated VCM, see, for example, Isaac and Walker (1988), Andreoni (1988b), Croson (1996), Andreoni and Croson (2008), Keser (2000), and Muller et al. (2008). Finally, Arifovic and Ledyard (2011) merge

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9. 10. 11. 12. 13. 14.

15. 16.

17. 18.

19. 20. 21.

22. 23.

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their individual evolutionary learning model with heterogeneous other-regarding preferences to capture the behavioral patterns commonly seen in the repeated VCM. See Andreoni, Gillen, and Harbaugh (2013) for a discussion of the power of revealed preference tests. Individual endowments range between 50 and 100 tokens; thus the margin of error is between 5% and 10% of the individual’s budget. That is, Afriat’s (1972) critical cost efficiency index is close to 1. This insensitivity to scope is similar to that seen in the contingent valuation literature (Kahneman 1986; Kahneman and Knetsch, 1992). See Korenok, Millner, and Razzolini (2013) and Deb, Gazzale, and Kotchen (2014) for extensions to models of impure altruism. The models of other-regarding preferences discussed in Cooper and Kagel (Chapter 4) can also help explain unconditional transfers. I refer to their chapter for discussion of the significant contributions on fairness and reciprocity (Bolton and Ockenfels 2000; Fehr and Schmidt 1999; Rabin 1993; Levine 1998; Dufwenberg and Kirchsteiger 2004; Falk and Fischbacher 2006), egocentrism (Cox, Friedman, and Sadiraj 2008), and efficiency (Andreoni and Miller 2002; Charness and Rabin 2002). Provided the individual remains a contributor (see Bergstrom, Blume, and Varian 1986). This finding is commonly referenced when demonstrating the weakness of the pure altruism model. As noted by Vesterlund (2006), this prediction relies on the somewhat unusual assumption that the individual’s demand for the public good does not increase with the increase in the population. That is, it implicitly relies on the assumption that the number of recipients and the need for the nonprofit’s output stays constant as the population increases. The result does not follow if the need for the public good increases at the same rate as the population. See also Cornes and Sandler (1984) and Steinberg (1987). Note that if the warm-glow of giving decreases with the recipient’s well-being (that is, the joy of giving decreases when the need for funds is small), then extreme free riding is also predicted in a model of impure altruism. See Andreoni, Harbaugh, and Vesterlund (2008) for a discussion of the role altruism plays across a series of different environments. See, for example, Carter, Drainville, and Poulin (1992), Saijo and Nakamura (1995), Palfrey and Prisbrey (1997), and Goeree, Holt, and Laury (2002). One set of treatments provides participants with one indivisible unit and asks them to either keep it in the private account or to place it in the public account. Another set of treatments provides participants with nine divisible units and asks them to allocate these between the private and the public account. See also Offerman, Sonnemans, and Schram (1996), who find evidence of warm-glow in a step-level public good environment. See, for example, Dana, Cain, and Dawes (2006), Dana, Weber, and Kuang (2007), and Andreoni and Bernheim (2009). With r i varying, the Palfrey and Prisbrey (1997) environment is also one of heterogeneous endowments. Studies using tax return or actual contribution data often estimate the effect of government contributions on individual giving. While this comparative static is informative for policy purposes, it cannot be used to draw inference on motives unless donors know how changes in government contributions influence giving by others (Vesterlund 2006) or without controlling for the fundraiser’s response to such changes (see, e.g., Andreoni and Payne (2003, 2011) and Zhang (2011) for examinations of the effect government grants have on fund-raising expenditure and on the resulting private contributions). An advantage of experimental studies is that they make it possible to control and manipulate the information individuals hold about overall provision, and secure that changes in individual contributions do not result from changes in solicitations. Chan et al. (2002) examine an environment similar to that of Andreoni (1993) but consider both a highand a low-tax treatment. While they replicate Andreoni’s results for the low- (and comparable-) tax treatment, they find complete crowd-out when the tax is large. They conclude that warm-glow fails to explain the result. Gronberg et al. (2012) note that an unfortunate consequence of the Chan et al. study is that the solution concept differs between the two treatments, with zero giving being a dominant strategy in the high-tax treatment. Relying on Keser (1996), they therefore alter the payoff such that there is a dominant strategy equilibrium in both treatments. They find, as in Andreoni (1993), that there is incomplete crowd-out. However, Sutter and Weck-Hannemann (2004) fail to replicate Andreoni’s initial crowd-out result. Using the same design, they see the same level of contribution in the tax treatment but find greater donations in the no-tax treatment. The resulting level of crowd-out is 97.5%, and they cannot reject that individuals are motivated solely by pure altruism.

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26. The crowd-out measures reported by Andreoni (1993) and Bolton and Katok (1998) do not account for the fact that contributions below the imposed contribution level cannot be fully crowded out. For example, in the Bolton and Katok case contributions of less than $3 in the $18/$2 treatment cannot be fully crowded out in the $15/$5 treatment. Failure to account for this truncation biases the results toward incomplete crowd-out. See Ottoni-Wilhelm, Vesterlund, and Xie (2014). 27. See also the Korenok, Millner, and Razzolini (2013) extension of Andreoni and Miller (2002), which determines if allocations can be rationalized by impurely altruistic preferences. While not examining budgets that allow for a test of crowd-out, they find that behavior by a majority of participants can be characterized by impurely altruistic preferences. A similar method is used in Deb, Gazzale, and Kotchen (2014). 28. While showing evidence of both warm-glow and altruism, the fMRI studies cannot shed light on the relative weight of these two motives. 29. Similarly, generosity toward one nonprofit need not be a good predictor of generosity to another. Few would be surprised to find that a generous contribution to Planned Parenthood does not predict a generous contribution to the National Rifle Association. Nor should we be surprised that an individual’s generosity in the laboratory does not extend to all domains. As a test of the external validity of lab experiments, Laury and Taylor (2008) use the VCM design of Goeree, Holt, and Laury (2002) to identify preferences for giving and to determine whether these predict the participant’s contribution to an urban tree-planting program. While the likelihood that someone contributes is correlated between the two environments, the parametric estimates of altruism do a poor job of predicting giving to the naturally occurring public good. More than evidence that the laboratory study fails to generalize this may be evidence that preference for giving depends on the characteristics of the public good. 30. In particular it has been suggested that contributions to nonprofits can be used to signal wealth (Glazer and Konrad 1996), prestige (Harbaugh 1998a, 1998b), or image (Holländer 1990; Bénabou and Tirole, 2006). 31. See also Broberg, Ellingsen, and Johannesson (2007) on the willingness to pay to opt out and Lazear, Malmendier, and Weber (2012) on the response to the cost of opting out as well as the effect this sorting has on the remaining contributors. Evidence of moral wiggle room is also seen in Linardi and McConnell (2011), who find that volunteering decreases when an excuse for not volunteering is introduced. In a field experiment, Andreoni, Rao, and Trachtman (2016) also find evidence of opting out as customers avoid doors to a supermarket where a solicitor for the Salvation Army is stationed. 32. The willingness to delegate to a nongenerous agent may result from the fact that the recipients do not, to the same extent, hold the decision maker accountable for the delegated outcome (Bartling and Fischbacher 2012; Coffman 2011). Extending research on delegation, Coffman finds that when gifts are raised through an intermediary, the likelihood of giving and the size of the gift are much less sensitive to the identity and quality of the charity. 33. Evidence that individuals respond to others observing their behavior is also seen in Haley and Fessler (2005), who document that a set of painted eyes induces more generous behavior in a dictator game. Similarly Bateson, Nettle, and Roberts (2006) examine contributions to pay for drinks in a university coffee room and find that, compared to a control image, an image of a pair of eyes almost tripled contributions. 34. In contrast to the field, laboratory studies on visibility generally restrict the inference that may be conveyed through a visible contribution. While contributions in the laboratory can be seen as a sign of generosity; models such as Glazer and Konrad (1996) suggest that donations also can serve as a signal on wealth. Bracha and Vesterlund (2013) show that the effect of visibility is not clear when contributions serve both as a signal on generosity and wealth/ability. When ability is not known, they find that visibility lowers the contributions by low-ability individuals. It appears that individuals prefer to be perceived as poor and generous rather than as rich and stingy. Evidence from the field also shows that visibility need not increase contributions; for example, Onderstal, Schram, and Soetevent (2013) do not find an increase in giving when individuals contribute using an envelope with their address versus an envelope without such an identifier. See Section 3.3 for further discussion. 35. Participants were Princeton undergraduate students. When asked to evaluate the two organizations, 92% of participants positively identify with the Red Cross while 72% negatively identify with the NRA. 36. See also Cox, Sadiraj, and Sadiraj (2008), who provides evidence of taking in a game when initial endowments are the same. 37. Harbaugh (1998b) shows that contributions to a large university increase when using coarse contribution recommendations. 38. To demonstrate that temptation can explain behavior, consider a case where a flyer announced the distribution of free ice cream. Few would conclude that the decision to opt out of getting free ice

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39. 40. 41. 42.

43.

44.

45. 46.

47. 48.

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cream can be seen as evidence that those who, without prior notice, are offered and consume the ice cream do so in response to social pressure. There is conflicting evidence on whether individuals are tempted to be generous or selfish; for example, Noor and Ren (2011) find that there is temptation to be selfish, and DeWall et al. (2008) find that depletion increases selfishness. By contrast, Rand, Greene, and Nowak (2012) examine response time in a VCM and find more-generous contributions by fast decision makers or by those who are forced to quickly contribute. They conclude that individuals intuitively are cooperative and that selfishness requires reflection. Subsequent studies, however, cast doubt on the Rand et al. conclusion; see, for example, Tinghög et al. (2013) and Kessler and Meier (2014). Recalde, Riedl, and Vesterlund (2013) find evidence to suggest that the negative correlation between giving and response time may result from mistakes being made quickly. Looking at contributions in a public good game with interior equilibria, they replicate the Rand et al. finding when the equilibrium is toward the bottom of the strategy space but get the reverse result when it is toward the top of the strategy space. As evidence that mistakes are made quickly, they find, in contrast to slow decision makers, that the contribution distribution for fast decision makers is independent of treatment. Fast decision makers are also shown to be significantly more likely to make mistakes that decrease both private and group earnings. The assumption of contribution maximization is equivalent to an assumption of provision maximization, provided production of the public good is monotonically increasing in contributions. Suppose, for example, that Ui = xi + αi ln G, i = 1, 2, and α1 >α2 , then equilibrium provision is G = α1 = g1 in the simultaneous game and G = α2 = g2 in the sequential game, provided α1 / α2 V, the trade does not execute and they get nothing. Importantly, no feedback about whether the trade occurred is provided to either player after each round. By regressing each buyer’s suggestions S against their values V, Bhatt and others could classify buyers into three types. One type showed no strong correlation. A second “incrementalist” type typically had a strong positive correlation (and high R 2 ) due to deliberate revelation of values (in an effort to increase efficiency). A third “strategist” type used a counterintuitive strategy of sending high S suggestions when they have low values V and sending low suggestions when they have high values (so S and V are negatively correlated). (This behavior is predicted as level 2 in a modified CH model.) The idea is that naïve level-1 sellers will attempt to make inferences about how “honest” a buyer is by considering the history of suggestions they see in the game. If those sellers see only low values of S, they will infer that the buyer is low-balling and will ignore the suggestions15 . However, if they see a relatively uniform mixture of suggestions, they will think the buyer must be prosocially revealing something about their values to increase gains from trade. They will tend to trust the suggestions, choosing low prices when they see low suggestions and high prices when they see high suggestions. Level-2 strategist buyers will realize this and use low-value rounds, where they don’t stand to earn much anyway, to generate credibility so that they can reap all the rewards from very low prices during the high-value rounds. Bhatt and others found that during the buyer’s price-suggestion period, there is stronger activity in the DLPFC for strategists compared to other subjects. This could be interpreted as evidence of active working memory (keeping track of the distribution of recent suggestions in order to make it look honest) or inhibition of a natural instinct to make suggestions that are positively correlated with value. There is also unusually large activity for strategists when they receive a high-value signal in STS close to the region observed in Hampton, Bossarts, and O’Doherty (2008) (and hence must bluff the most by suggesting a low price). For sellers who are judging how much information is conveyed by a buyer’s price suggestion, Bhatt and others (2012) found that activity in bilateral amygdala was correlated with a seller’s “suspicion,” as measured by how closely the seller’s price offers matched the buyer’s suggestions. A low correlation indicates suspicion and is associated with amygdala activity, consistent with an established role of amygdala in rapid vigilance toward threat (e.g., fear response).

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Together, these studies show that there is some match between computations inferred from choices (influence value and “strategizing”) and regions thought to be involved in value calculation and mentalizing, and in emotional judgments associated with economic suspicion. Montague and several colleagues have explored many aspects of a 10-period repeated trust game using fMRI. King-Casas and others (2005) found signals in the caudate nucleus of the trustee brain in response to positive (“benevolent”) reciprocity by the investor. This suggests the brain is computing a rather complex kind of social reward based on an anticipation of future responses. In addition, there is evidence that activity in the caudate region occurs earlier and earlier across later rounds of the experiment, by about 14 s, signaling a behavioral “intention to trust” well ahead of the actual behavior. More recently, Montague’s group has used trust games as a tool for doing “computational psychiatry”—that is, exploring how disorders are associated with disruption of conventional neural computations that are typically adaptive. King-Casas and others (2008) consider behavior and neural activity during the trust game in subjects with borderline personality disorder. Borderline personality disorder (BPD) is characterized by emotional disregulation, including some level of paranoia, often leading to unstable personal relationships. In the King-Casas experiment, subjects with BPD were paired as trustees with healthy investors matched on education, IQ, and socioeconomic status, and played 10 rounds of the trust game. The major behavioral finding is that pairs that included a BPD subject earned significantly less money in total than those involving two healthy subjects. This appears to be due to markedly lower levels of investment in the later rounds of the game by investors when playing with a BPD trustee. In healthy pairs, breakdowns of cooperation were often followed by “coaxing” behavior by the trustees: trustees would repay all or most of the money they receive during the trial. This signaled trustworthiness to the investor and often restored a cooperative interaction. Investments appeared to decrease in these pairs because BPD subjects failed to effectively signal their trustworthiness to the investors via this coaxing behavior. The study found that people with BPD had significantly decreased activation in the anterior insula (aIns) in response to low investments as compared to controls. Activity in aIns has often been linked to subjects experiencing emotional discomfort, perhaps accompanying a violation of social norms (e.g., low offers in the ultimatum game; Sanfey et al. 2003). A lack of activity here when BPD subjects see low investment suggests a failure to interpret those low investments as a lack of trust in response to trustee norm violations. The authors hypothesize that this failure to detect a violation of social norms impairs the ability of the BPDs to respond appropriately with coaxing. In turn this failure to coax leads to decreased cooperation throughout the experiment and fewer returns to both parties. Chiu and others (2008) find that autistic subjects had much weaker signals in regions of cingulate specialized to “self” signals about payoffs and actions of oneself. 6.5 Discussion of Strategic Neuroscience As noted in the introduction, the goal of neuroeconomics is not to find a special brain area for each task. Quite the opposite: the hope is that common patterns of circuitry will emerge that will inform debates about the computations that are performed and suggest new theories of behavior and new predictions. Strategic neuroscience is just beginning, but there is some tentative convergence about activity in four regions across studies: mPFC, DLPFC, the precuneus, and the insula. The locations of activity described in this section are identified in three brain “slices” and shown in Figure 3.7.

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DMPFC and Precuneus

x=5

Bhatt & Camerer 2005: Nonequilibrium choice Coricelli & Nagel 2009: Higher strategic IQ Hampton et al., 2009: Expected influence reward Kuo et al., 2009: Dom. solve vs. coord. Yamada et al., 2010: Sympathy in mitigation Young & Saxe 2009: Mental states in stories

(b) x = 35

Insula Chang et al., 2011: Guilt avoidance Hsu et al., 2008: Unfairness Kuo et al., 2009: Dom. solve vs. coord. Singer et al., 2006: Empathizing Tabibnia et al., 2008 Accepting unfair offers Yamada et al., in revision: Sympathy in mitigation

Figure 3.7: Regions of activity in various game theoretic and mentalizing tasks. (a) Sagittal slice from back (posterior) to front (anterior) of the brain, x = 5, showing activity in precuneus/posterior cingulate (posterior) and dorsomedial prefrontal cortex (DMPFC; anterior). (b) Sagittal slice, x = 35, showing activity in right insula. (Left insula regions are inverted to opposite right regions for purposes of plotting.) (c) Coronal slice from left to right, y = 24. Shows activity in dorsolateral prefrontal cortex (dlPFC).

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DLPFC

y = 24 Bhatt et al., 2009: Level 2 deception Coricelli & Nagel 2009: Higher strategic IQ Guroglu et al., 2009: Ultimatum rejections Kuo et al., 2009: Dom. solve vs. coord. Yoshida et al., 2009: Level of strategic thinking

Figure 3.7: Continued

mPFC. Activation in dorsal mPFC was found when choices were out of equilibrium (Bhatt and Camerer 2005) among higher-level thinkers (Coricelli and Nagel 2009), when the other player’s sophistication is uncertain (Yoshida, Dolan, and Friston 2008), and when computing influence value (Hampton, Brossaerts, and O’Doherty 2008). This region is active in many social cognition tasks, including self-knowledge and perspective taking (Amodio and Frith 2006; D’Argembeau et al. 2007) and in some nonsocial tasks that require cognitive control (Ridderinkhof et al. 2004; Li et al. 2006). Amodio and Frith (2006) hypothesize that the region is involved with modulating behavior based on anticipated value, with the most posterior areas dealing with simple action values and representations getting increasingly abstract and complex moving forward toward the frontal pole. There is very tentative evidence consistent with this hypothesized posterior-anterior value complexity gradient, as measured by the y-coordinate in xyz-space.16 The simplest behavior is probably in Bhatt and Camerer (y = 36), two-step thinking is a little more complex (Coricelli and Nagel 2009, y = 48), and influence value is rather complex (Hampton, Brossaerts, and O’Doherty 2008, y = 63). dlPFC. The dorsolateral PFC is thought to be involved in working memory (which is necessary for doing “I think he thinks . . . ” types of calculations) and also in inhibition of rapid prepotent responses (such as implementing patient plans (e.g., McClure et al. 2004, 2007) and resisting tempting foods (Hare, Camerer, and Rangel 2009)). In the studies in this section, activity in the dlPFC is seen in Bhatt and Camerer (strategic choice out of equilibrium), Coricelli and Nagel (correlated with higher-level thinking), Yoshida and others (higher-level thinking), and Bhatt and others (strategizing price suggestions in bargaining). These results suggest dlPFC may be necessary for a combination of working memory and executive control required to play strategically at high levels. Importantly, Knoch and others (2009) found that application of disruptive TMS to right dlPFC reduced the tendency of players to build up reputations in

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partner-matching repeated-trust games (with no such change in anonymous strangermatching games). Precuneus. Precuneus activity is seen in Bhatt and Camerer (2005), Kuo and others (2009), and Bhatt and others (2010). The precuneus has reciprocal connections with many of the other areas mentioned throughout this chapter, including the mPFC, the cingulate (including both the ACC and retrosplenial cortices), and the dorsolateral prefrontal cortex. The precuneus has been implicated in a host of tasks, including episodic memory retrieval (Shallice et al. 1994, Fletcher et al. 1995, Lundstrom et al. 2003, Addis et al. 2004), attention guidance and switching both between objects and among object features (Culham et al. 1998; Le, Pardo, and Hu 1998; Nagahama et al. 1999; Simon et al. 2002), a variety of imagery tasks (Cavanna and Trimble 2006), and perspective taking (Vogeley et al. 2004; Vogeley et al. 2001; Ruby and Decety 2001). Precuneus is also one of the “default network” areas that are unusually active when subjects are conscious and resting (Raichle et al. 2001). Our hunch is that it is unlikely that the precuneus plays a special role in strategic thinking. Instead, the activity observed in a few studies is likely to be due to the fact that attentional control and perspective taking are important for complex strategic valuation. A fruitful way to learn more would be to vary a single dimension of games, such as symmetry versus asymmetry, which are designed to require more perspective taking and attentional control, and see if precuneus is actually more active. Insula. Insula activity appears in Bhatt and Camerer (correlated with low strategic payoff and accuracy) and Kuo and others (2009; correlated with focality in matching games). The insula is thought to be responsible for “interoception,” that is, the perception of one’s own internal state. It has been proposed that the information received in the posterior insula is processed and rerepresented in the anterior insula as subjective emotion and is also important for a feeling of self (Craig 2002; Critchley 2005; Keysers and Gazzola 2007). It may be that middle-insula activity reflects more basic visceral sensations in these games—like intuitive impulses corresponding to generalized strategic uncertainty rather than to more analytical processing. (Note the well-established role of insula in encoding financial uncertainty, discussed in the section Risky Choice in this chapter.) 6.6 Summary Game theory has emerged as a standard language in economics and is the focus of thousands of behavioral experiments. So far, a small number of fMRI studies and several studies using variants of eye-tracking are reasonably supportive of cognitive hierarchytype models as models of both mental computation and initial choices. Game theory has also influenced social neuroscience by providing paradigms and predictions (e.g., Rilling and Sanfey, 2011). Given that there is a huge space of possible theories covering strategic thinking, learning, and teaching (or influence), it may be difficult to rapidly figure out which theories predict best and under what circumstances, using only choices. Theorists and experimenters struggle to find games and treatments that can separate (or identify) distinctive predictions of theories. If theories of strategic choice are described in terms of what cognitions and emotions are neurally computed to implement those choices, then competing theories could—in principle—be more efficiently distinguished using a combination of choice and neural data than using choice data alone. Substantial progress using the combination of choice and information search data has already been made in

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several studies. In addition, since many of the candidate brain regions identified so far in fMRI are close to the cortical surface (such as TPJ, dmPFC), other tools such as EEG and TMS, which record or disrupt electrical activity close to the cortical surface, could prove particularly useful in checking robustness of results from fMRI and lesion studies. Finally, it is useful to ask again—why care about where? That is, suppose we believed (with more confidence than we have now) that the common areas shown in Figure 3.7a–c are computing aspects of strategic value or action. What can be done with that information? The answer is that we can couple knowledge of function in these regions with emerging knowledge of how these regions work in different species, develop across the human life cycle (both childhood tissue growth and decline in aging), are connected to other regions, and are affected by gene expression, neurotransmitters, and drugs. Combining functional and anatomical knowledge will lead to predictions about the types of animals and people who may behave more or less strategically. Predictions can also be made about how activity will be modulated by changes in representations or simply environmental effects, which either overload or activate these regions.

7 CONCLUSION This chapter reviews the nascent, rapidly growing literature in neuroeconomics, paying particular attention to experimental methods. There are five principal motivations for pursuing neuroeconomic research. First, some researchers—even some economists—are willing to study neuroscience for its own sake. Second, neuroeconomic research provides a new way of imperfectly measuring human well-being. Third, neuroeconomic concepts serve as catalysts for model development. Fourth, neuroeconomic methods provide a new, powerful way to test economic models that ambitiously specify both how choices depend on observables and what computational mechanism leads to those choices. Fifth, neuroeconomics will improve our ability to predict behavior and to design interventions that (1) influence the behavior of others and (2) manage our own appetites and drives. This chapter focused on two methodology topics—basic neurobiology and neuroimaging—and four applications—risk preferences, intertemporal choice, social preferences, and strategic behavior. Many other important topics needed to be omitted for lack of space. Active work in neuroeconomics is taking place in every choice domain. Even blindfolded, a pedestrian could walk across a college campus. But that person would travel more efficiently with full use of his or her senses. Likewise, economists should remove our own methodological blindfold. At the moment, the cost of wearing a neuroscientific blindfold is not great, since neuroscience is in its infancy. However, as neuroscience methods continue to rapidly advance it is likely that neuroscientific insights will significantly improve our economic vision.

ACKNOWLEDGMENTS We gratefully acknowledge research assistance from Colin Gray and Gwen Reynolds and key guidance from John Kagel, Alvin Roth, and an anonymous referee. We also acknowledge financial support from the Moore Foundation (Camerer), the National Science Foundation (Camerer), and the National Institute of Aging (Cohen; Glimcher, R01AG033406; Laibson, P01AG005842), the Swiss National Science Foundation (Fehr, CRSII3_141965/1) and the European Research Council (Fehr, 295642).

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NOTES 1. Neurotransmitters are molecules that carry neurochemical signals from one neuron to another. 2. Other neuroimaging methods include magnetic resonance imaging (MRI), positron emission tomography (PET), and electroencephalograms (EEG) 3. See Colander (2007) and Edgeworth (1881, 101). 4. Discrete choice models (e.g., Logit) have alternatively been interpreted as models with decision noise, like game-theoretic trembles, or models in which true utility has a stochastic component. In fact, these perspectives are both sensible and mutually compatible. 5. Becker and Murphy (1988) conjecture: “People get addicted not only to alcohol, cocaine, and cigarettes but also to work, eating, music, television, their standard of living, other people, religion, and many other activities.” Within their model, “addiction” is simply adjacent complementarity in consumption (marginal utility is increasing the level of past consumption). However, to a neuroeconomist, addiction to drugs is a biological process marked by changing synaptic function, changing reward prediction error, increasing tolerance, withdrawal upon cessation, craving, and sensitivity to environmental cue “triggers” associated with past use (Laibson 2001). So the economic and neuroeconomic approaches can be distinguished empirically. Becker and Murphy’s claim about the breadth of their theory could then be tested on a neuroeconomic basis (along with choices and prices). 6. Note how obviously cardinal and linear is this discussion of firing rates as encoding schemes. To a neurobiologist, who is essentially an algorithmic engineer, this is the most natural way to imagine firing rates. Perhaps somewhat surprisingly, there is also a huge amount of data to support the conclusion that firing rates actually are often linear with important environmental variables. Perhaps even more surprisingly, the activity level of a given neuron during rest actually does correspond, in most cases, to the default state of the variable being encoded. One simple example of this is the representation of the speed of a moving object in the visual system. Within a fixed range of speeds for each neuron, firing rates in cortical area MT are highly linear encoders of this highly abstract property, with almost all variance accounted for by the Poisson structure of fixed neuronal noise (Maunsell and Van Essen 1983, Tolhurst et al. 1983). 7. 5HTT appears to be associated with neuroticism and with depressive reactions to life events. However, it is important to note that associations of single gene polymorphisms with broad behavior generally do not replicate strongly from study to study. As a result, the trend in “genoeconomics” is toward GWAS sampling of large numbers (500,000 +) of candidate genes, with aggressive correction for multiple comparison to avoid false positives. The Roiser et al. (2011) study chose to look at 5HTT specifically because of the role of amygdala shown by fMRI in the earlier De Martino et al. (2006) study and because of other evidence of a link between 5HTT and amygdala. In any case, it is reasonable to be skeptical of any single gene-behavior association until at least five to ten studies find similar results. 8. Note that Tom et al. first identified regions that were responsive to both increased gain and reduced loss (by looking at all brain areas, a “whole-brain analysis”) and then measured whether individual differences in the BOLD signal in one of those regions (chosen a priori) correlated with different individual λ values estimated from choices. This procedure avoids an important critique articulated by Vul et al. (2009)—that cross-individual correlations between fMRI activity and behavioral measures are likely to be implausibly high if they result from a whole-brain search (see also commentary on the Vul paper in the same journal, and Kriegeskorte et al. 2009). 9. These types of causal influences have been using pharmacology and techniques like TMS to affect vision and motor movements for a long time. 10. This section draws heavily on (and overlaps with) the work of Fehr and Camerer (2007) and Fehr (2009). Interested readers can find details in those papers. 11. Transcranial direct current stimulation. 12. See Camerer et al. 1993; Nagel 1995; Stahl and Wilson 1995; Costa-Gomes, Crawford, and Broseta 2001; Camerer, Ho, and Chong 2004; Crawford et al. 2013. 13. Being “in equilibrium” is defined behaviorally as trials in which choices are best responses to beliefs, and both beliefs and second-order beliefs match choices and beliefs of other players. If players are rational (best-responding) and think others are rational, these belief-matching constraints are sufficient for Nash equilibrium. 14. Notice that while these theories can be difficult to distinguish using only observed choices, it is easy to distinguish them with cognitive data: adaptive players do not need to look at the payoffs their opponents get, but sophisticated players do need to look at those payoffs. The fact that players usually do attend to payoffs of others players (e.g., Knoepfle, Wang, and Camerer 2009) is evidence for sophistication.

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4 Other-Regarding Preferences A SELECTIVE SURVEY OF EXPERIMENTAL RESULTS

David J. Cooper and John H. Kagel

INTRODUCTION There has been an enormous amount of experimental research devoted to “otherregarding preferences” since the publication of the first Handbook of Experimental Economics (Kagel and Roth 1995). This literature’s daunting size poses serious problems in terms of developing a survey since it is necessary to ignore (or only mention in passing) many worthwhile experiments, along with the flood of results that will no doubt be published shortly after this survey is completed.1 The literature has also yielded a number of theoretical models designed to organize the data—a search for meaning based on the “facts”2 —making this an area of experimental research where theories flow directly from the experimental outcomes (as opposed to the more usual case of experiments designed to test extant theory). As such one must choose a point of attack to get through the literature—should it be theory or data driven? The one adopted here is “historical,” using the results of a series of experiments conducted by different groups, often designed to test the latest theories used to explain earlier data. We start with a brief review of where things stood at the time the first Handbook of Experimental Economics was published. We then introduce the two theory papers that have had an enormous influence on this literature, Bolton and Ockenfels (BO; 2000) and Fehr and Schmidt (FS; 1999). These papers showed how other-regarding preferences over income inequality could explain a large number of experimental outcomes, usually in small-group bargainingtype environments, which the “standard” economic model of strictly selfish preferences failed to organize. In contrast, the same preferences, under different institutions (e.g., competitive markets) produced the standard results. All this was done without the need to ignore too many “dead rats” (extant results that contradict one or the other of the two models). This led to a burst of new experiments designed to distinguish between concerns for income inequality on which the BO and FS models focused and other issues such as intentionality and efficiency. We then review some of newer models designed to incorporate these experimental findings, as well experiments responding

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to these newer theories (e.g., Charness and Rabin 2002). Much of the focus here will be on bargaining games (especially the ultimatum game) and the dictator game. While most of the literature has focused on models that rely on modifying players’ utility functions to explain other-regarding behavior, there is also a strand that uses adaptive learning models for this purpose. We briefly digress to describe these papers since they not only provide an alternative explanation for some of the experimental results but also helped to spur the experimental learning literature (see Chapter 10 on learning). We devote a separate section to “gift exchange” experiments, both because they have a different structure from bargaining and ultimatum games and have recently been the subject of heated debate. It should be clear by the time we finish this survey that there is no single, all-encompassing model able to consistently explain all of the experimental results relating to other-regarding preferences and that a tractable model of this sort is unlikely to emerge any time soon. At this point in time there are a number of surveys dealing with the other-regarding preference literature that the interested reader might wish to consult. Fehr and Schmidt (2006) and Camerer (2003) cover much of the experimental literature up to their point of publication. Rotemberg (2006) surveys reciprocity and altruism in the workplace (field data), results of which are particularly relevant to the gift exchange literature.

I WHERE THINGS STOOD CIRCA 1995 Much of the work on other-regarding preferences in 1995 hinged on results from ultimatum and dictator games.3 In the ultimatum game two players, 1 and 2, must decide how to divide a sum of money, k, between them. Player 1 (the Proposer) makes an offer to player 2 (the Responder), which if accepted is divided as player 1 proposes. However, if player 2 rejects the offer, both players get nothing. Although there are many Nash equilibria in this game, the subgame perfect equilibrium outcome in which player 1 offers the minimum amount of money required (or a small positive amount in case of no minimum requirement) is a natural equilibrium refinement under the “standard” assumption that players care only about own income. In contrast to this prediction, Proposers in developed economies typically offer between 40% and 50% of the pie, which Responders accept. Smaller shares are usually rejected with sufficient regularity that Proposers’ income-maximizing offer is in the neighborhood of 40% to 50%.4 The beauty of this sequential bargaining game is that you get to see the Responder’s choice in every game, and Responders face no game-theoretic issues, such as ability to do backward induction or concerns about strategic uncertainty.5 These initial experiments involved relatively small sums of money—$10 to $30. Left unresolved was the issue of robustness, as one might suspect that with larger sums at stake, the amount that Responders would require to accept a proposal will go up, but the percentage of the pie required might well go down. There are effects of this sort, with substantial deviations from the subgame perfect equilibrium outcome continuing to be observed. For example, Slonim and Roth (1998) conducted an experiment in the Slovak Republic where modest stakes (by American standards) had large purchasing power. They compared games in which the amount of money at stake in terms of local purchasing power equaled $30 in terms of US purchasing power, one month’s average wages in the Slovak Republic, or three month’s average wages. Their data show rejection rates decreased as the amount of money at stake increased, falling from 26% under the smallest stakes to 14% with the largest (pooling over all offers strictly less than half the

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pie). Although this decrease may not seem large, it is statistically significant. Learning by Proposers was more rapid in games with high stakes—subjects who initially made high offers reduced their offers more rapidly, while those who initially made low offers raised them more quickly than in their other treatments. Nevertheless, the mean share of the money offered changed very little, averaging 45% of the pie with the smallest stakes to 43% of the pie with the largest stakes and with median offers staying in the 41% to 50% range throughout. Cameron (1999) reports similar results from Indonesia, with the amount of money at stake ranging from a day’s wages to a month’s wages. She found no significant change in the Proposer’s behavior with increased stakes but observed lower rejection rates in the higher-stakes treatments. Controlling for differences in the distribution of offers, rejection rates were estimated to be 17% lower in the highest-stakes treatment than in the lowest-stakes treatment. This experiment ran for only two rounds, so there is not much that can be said about learning. Rustichini and others (2012) offer a more extreme variation on stake size, with the highest stakes being a thousand times higher than the lowest stakes. The instructions for Proposers include language designed to generate an unusually high fraction of low offers, making it easier to detect changes in the willingness of Responders to accept small offers. Their data set indeed contains a high proportion of low offers. As stakes go up, the percentage of the pie offered to responders decreases but not as much as the stakes increase so that the amount offered actually increases. Even with large stakes and coaching Proposers to make low offers, proposer behavior is not consistent with the perfect equilibrium. With the highest stakes, rejections largely vanish (1 of 24 offers is rejected), even though more than three-quarters of the proposers offer less than 20% of the pie. To interpret this result, it helps to understand that artificially depressing offers makes stakes effects look larger since relatively generous offers (which are almost always accepted under all stakes conditions) become a small portion of the dataset. For example, suppose we limit the Slonim and Roth data to offers in the bottom quartile (offers less than or equal to 40% of the pie). The decline in rejection rates now looks much steeper with a drop from 40% with the lowest stakes to 17% with the highest stakes. Leading models of other-regarding preferences, such as the Rabin (1993) and Bolton and Ockenfels (2000) models discussed later, predict that rejections will largely vanish as stakes get sufficiently high since even a small share of the pie results in a large offer. Rustichini and others don’t offer a major departure from the previous literature. They push the literature to its logical extreme, and find results that are consistent with the existing theoretical and empirical literature. One of the key questions these ultimatum game results left open was whether the close to equal splits offered were a result of Proposers “trying to be fair to Responders” or were strategic responses to anticipated rejections of low offers—the expected payoff maximizing offer in ultimatum game experiments is typically around 40% to 50% of the pie. To sort out between these two alternatives, Forsythe and others (1994) compared ultimatum and “dictator” games. Like the ultimatum game, the dictator game is a twoplayer game in which player 1 (the dictator) proposes to split a fixed sum of money with player 2. However, unlike the ultimatum game, in the dictator game player 1’s proposal is binding, with player 2 having no say in the matter, as both players receive whatever the dictator proposes. This eliminates any strategic considerations from the dictator’s offer and resulted in a dramatic downward shift in offers compared to the ultimatum game: The modal offer changed from a 50–50 split in the ultimatum to game to a zero

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offer in the dictator game (see Figure 4.1). Nonetheless, offers in the dictator game were not all zero (or close to it) as one would expect if own income were all that mattered for dictators and there was a cluster of equal splits.6 The contrast between dictator and ultimatum game results clearly indicate that strategic considerations (anticipation of rejection of low offers) underlies the near equal splits typically reported in ultimatum games. At the same time they suggest some concern for the well-being of others. There have since been a large number of dictator type experiments designed to sort out between various hypotheses concerning the nature of subjects’ other-regarding preferences. These are discussed in Section III.F along with experiments demonstrating the sensitivity of the experimental outcomes to rather modest changes in experimental procedures. Just as it wasn’t initially clear whether Proposers’ behavior in the ultimatum game was driven by distributional or strategic concerns, it also wasn’t obvious whether the rejection of positive offers was due purely to outcomes or reflected a desire to punish unkind actions by Proposers. Blount (1995) was one of the first to show that intentions matter as she compared ultimatum games in which human Proposers made offers to games in which it was common knowledge that the proposals were generated (1) by a computer and (2) by a “disinterested” third party. Using the strategy method, she elicited minimum acceptable offers (MAOs) from all subjects prior to their knowing if they would be randomly assigned to the role of Proposer or Responder. Figure 4.2 reports her results, which yield statistically significant differences between the random treatment and either the standard (“interested party”) treatment or the third-party treatment, but no significant differences between the latter two treatments.7 An interesting sidelight to this paper consists of a follow-up study in which she repeats the exercise under conditions where (1) subjects knew they would be assigned

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to the role of Responder and (2) they were shown the distribution from which offers will be drawn. In this treatment there was a large, statistically significant, increase in the frequency with which subjects were willing to accept the lowest possible offers ($1 or less) in the “interested party” treatment.8 Blount attributes this difference to the fact that subjects knew their role prior to deciding, and that “the proposal was contained in an envelope attached to their packet of materials, which led them to reason through the problem in a slightly different manner taking a much more directly self-interested approach” (Blount 1995, 138). Much of the post-1995 literature on other-regarding preferences has centered around explicit models. The roots of all the major models lie in papers written prior to 1995. One thread of the theory literature focuses on preferences over the distribution of payoffs across players. The idea that subjects’ utility functions should include a distributional component is a relatively old one. The earliest example we are aware of that explicitly discusses how subjects’ utility function ought to be modeled is Ochs and Roth (1989). They study a rich set of alternating offer bargaining games and find strong departures from the standard theory of self-regarding preferences

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combined with subgame perfection. The most striking feature of their data is the frequency of disadvantageous counteroffers. When players reject an offer, 81% of their counterproposals give them less money than they just turned down. These subjects are actively taking less money in exchange for a more even distribution of payoffs. Ochs and Roth’s discussion of these results focuses on how subjects’ utility functions must be modified to capture this anomalous behavior: “uncontrolled elements of utility include some component that measures ‘unfairness’ as deviations from equal division . . . which takes the form of a minimum percentage” (Ochs and Roth, 377–78). Bolton (1991) took the next major step in the development of this literature. He also studies behavior from a series of alternating-offer bargaining games. To organize the anomalous behavior of subjects, Bolton presents an explicit model of subjects’ utility functions that includes the proportion of their payoff to the other player’s payoff as an argument. This model differs from its better-known successor, Bolton and Ockenfels’ (2000) ERC model, on a number of technical dimensions—the functional forms are different, the earlier model is a complete information model, and the earlier model is not designed to capture aversion to advantageous inequality—but possibly the most important difference is one of purpose. Bolton (1991) aims to explain behavior from bargaining games, but Bolton and Ockenfels (2000) have more universal goals, attempting to explain behavior from a wide variety of games, including examples where subjects don’t seem to exhibit other-regarding behavior. Rabin (1993) represents a markedly different approach to modeling other-regarding preferences. Drawing on psychological game theory (Geanakoplos, Pearce, and Stacchetti 1989; Battigalli and Dufwenberg 2009), Rabin’s model gives a central role to beliefs. The theory revolves around the concept of “kindness.” Player j ’s kindness to player i is given by the (normalized) difference between player i ’s expected payoff and an “equitable payoff,” as determined by player i ’s beliefs about player j ’s actions and player j ’s beliefs about player i ’s actions (second-order beliefs). Based on this technical definition of kindness, the utility function then states that players are more willing to be kind to others who they expect to be kind to them. The critical innovation is that preferences don’t depend solely on outcomes, but also depend on what other options were available and second order beliefs. The model is elegant in the extreme and captures important aspects of reciprocity, but is not terribly tractable and can yield implausible equilibria.9

II MODELS OF OTHER-REGARDING PREFERENCES, THEORY, AND TESTS A Outcome-Based Social Preference Models The pioneering work of Fehr and Schmidt (1999) and Bolton and Ockenfels (2000) focused on models of players’ concerns about the distribution of payoffs, along with their own income, to help explain ultimatum and dictator game outcomes. The real beauty of these two papers is that through simply adding concerns about the distribution of payoffs to standard concerns about one’s own income, they were not only able to make sense of dictator and ultimatum game outcomes in which standard “selfish” economic man fails to be revealed, but they also showed, without changing the structure of preferences, that standard own-income-maximizing results emerged in different environments. All this was done while not needing to ignore much, if anything, in the way of inconsistent results. Both sets of authors fully recognized that other “fairness” considerations, particularly intentionality and reciprocity, were likely to play a role in

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experimental outcomes but limited themselves to features needed to organize the main stylized facts at the time. In short, what these two papers did was to summarize the emerging other-regarding behavior results up to that point in time, including results from gift exchange experiments, and by explicitly modeling this behavior, set off a whole new round of experiments that have helped to clarify the nature of these other-regarding preferences. The Fehr-Schmidt (FS) and Bolton and Ockenfels (BO) models assume that the utility ui (x) of an outcome x = (x1 , . . . ,xi , . . . ,xn ) for a player in the game depends on player i ’s own payoff xi as well as how it compares to other players’ payoffs. Some percentage of individuals in the population are assumed to get negative utility from having lower payoffs than others, which explains why Responders are willing to reject low, but positive, income offers in the ultimatum game. Once Proposers recognize this, they respond by making substantial positive offers, as observed in the data. There is also a portion of the population that gets negative utility from being better off than others, which can explain the positive offers in the dictator game. Both models assume that the disutility from being worse off than others is likely to be greater than the disutility from being better off. A nice feature of both models is that heterogeneity is explicitly accounted for by assuming a distribution of preferences in the population. Even with a majority of players having standard preferences—concern for own income only—both models can explain the results from ultimatum and dictator games. Both models are fairly tractable since players’ preferences depend only on the outcomes of the game and not on how they have been achieved. It is therefore easy to apply both models and to make predictions about new games. An interesting feature of both models is that they implicitly ignore payoffs outside the laboratory. This amounts to an assumption that wealth outside the lab is the same between subjects or is irrelevant to decisions made inside the lab. This assumption may seem innocuous, but it may be important for experiments that study interactions between differing ethnic groups (e.g., Fershtman and Gneezy 2001).10 Formally, both models assign utility based on a subject’s own payoff and an otherregarding component that compares a subject’s payoff with the payoffs of others. In the FS model, this social comparison function is based on the difference between subjects’ own payoff xi and the payoffs of all other subjects in the game. Utility is reduced when i ’s payoff is either higher or lower than other subjects’ payoffs, with the reduction being greater in the second case. The resulting utility function is shown in (1). The parameters αi and βi capture the marginal disutility from disadvantageous and advantageous inequality—by assumption αi ≥ βi ≥ 0. It is important to note that the summations in (1) cannot be replaced with the average payoff to others, as the distribution of payoffs over others affects the utility function. A second critical point is that the utility function is not assumed to be identical for all individuals. FS take advantage of this feature in exploring how the model can explain data from a variety of experiments. While the FS model is linear, there is no particular reason it cannot be modified to be nonlinear.     1 1 max |x j − xi , 0| − βi max |xi − x j , 0| ui (xi , x−i ) = xi − αi n − 1 j =i n − 1 j =i (1) In the BO model, the social comparison function is based on the proportion of total payoffs a player receives. Holding own payoff fixed, utility is maximized when an individual’s payoff is equal to the average payoff over all individuals. The functional form of the utility function is shown in (2). Note that the model assumes that all

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payoffs are nonnegative. Unlike FS’s model, the BO model explicitly allows for nonlinear preferences. ui (xi , x−i ) = v (xi , σ (xi , x−i )) xi σ (xi , x−i ) = n

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From a practical point of view, the two models make similar predictions in spite of their differing functional forms. The FS model can be sensitive to changes in the distribution of payoffs over other individuals (as opposed to changes in the average payoff of other individuals), which do not affect predicted behavior under BO. Consider a distribution of strictly positive payoffs over three players, P1, P2, and P3. Now imagine that a constant k, where 0 < k < min[P1, P2, P3], is added to P3’s payoff and subtracted from P1’s payoff. Under BO, this cannot impact P2’s utility because his or her payoff share is unaffected. With the FS model, this will lower (raise) P2’s utility if the original payoffs are strictly increasing (decreasing) in the player indices. The BO and FS model also make slightly differing predictions as more players are added to the game, an issue that we discuss shortly in the context of three-person ultimatum games. Remarks. The BO and particularly the FS models have been met with a number of criticisms. We leave the issue of intentions and reciprocity aside for the moment. BO and FS both made it clear that they understood these factors to be present. Their models are not intended to be complete theories of all factors involved in other-regarding behavior and, therefore, do not incorporate features that are unnecessary to rationalize the existing data. Experiments designed to better understand the role of intentions and reciprocity are discussed in detail in the next section. Rotemberg (2008) notes that both BO and FS have trouble explaining the common use of even splits in the ultimatum game. The point is actually easier to see in terms of dictator games, which also have an atom at the even split. BO predict that there should be no even splits in the dictator game since the marginal utility from own income is positive at an even split and the marginal utility from the other- regarding component of the utility function is zero. FS rationalize even splits in the dictator game (as well as the ultimatum game) in terms of β > ½, so that individuals strictly prefer a dollar in the pocket of someone with lower income than themselves to a dollar in their own pocket. Rotemberg argues that this represents an implausibly high level of altruism and also notes that introducing a nonlinear utility function in place of the piecewise linear function does not improve matters. He then offers a model in which Responders treat low offers as a signal of strong selfishness on the part of Proposers that they want to punish. That is, like FS and BO Rotemberg explains rejections of unequal splits in the ultimatum game in terms of ill will toward Proposers but argues that the ill will is not a result of income inequality. Shaked (2006) offers a much more sweeping indictment of the FS model. The argument can be summarized as follows: By virtue of having an infinite number of possible parameters’ values, the theory can predict a wide range of outcomes, from the competitive to the cooperative, so that its predictions depend on the value of these parameters. (The infinite number of parameters’ values referred to concern the heterogeneity of preferences within any given sample population, so that for any given game the theory’s predictions depend on how inequity averse the population is.) As

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such, the theory has no explanatory value beyond the capacity to predict a broad range of outcomes as a function of possible parameter values within a given population. We agree that there clearly are problems with both the BO and FS models, but holding these models to their point predictions is probably too stringent a standard. Even in settings where intentions and reciprocity have little force, any attempt to have a single functional form fit the infinite variety of preferences present in the population is bound to lead to some questionable results. The mass at the even split in dictator game makes this point clear. As Andreoni and Bernheim (2009) argue persuasively, these individuals are probably following a social norm with the goal of appearing “fair” rather than maximizing a well-behaved utility function over the distribution of payoffs. In other words, the behavior of these subjects is driven by objectives outside the realm of any model of purely outcome based preferences. What BO and FS did quite successfully is to provide a tractable model that can rationalize and synthesize a reasonably large body of data. Their work also motivated a large number of new experiments designed to better understand what drives deviations from the standard (strictly) selfish preference model. B Some Initial Tests of the Bolton-Ockenfels and Fehr-Schmidt Models Initial tests of the BO and FS models focused on two issues: (1) the extent to which choices depend not only on outcomes but also on how those outcomes were achieved (i.e., the extent to which reciprocity and perceived intentions play a role in these games) and (2) the scope of players’ concerns for own income compared to others in the relevant reference group. Falk, Fehr, and Fischbacher (FFF; 2003) investigated the role of intentions (or, more specifically, menu dependence) in a series of four discrete “mini” ultimatum games in which the Proposer chose between two possible allocations x and y. In all four games the reference point allocation x was the same: an (8, 2) split, where the Proposer’s share is listed first. In one game the alternative allocation was a (5, 5) split, compared to which the (8, 2) allocation is relatively selfish. In the second and third games, the (8, 2) split was paired with a (10, 0) division and a (2, 8) division, respectively. Compared with a (10, 0) option, the (8, 2) split is relatively fair, with the (2, 8) division forcing the Proposer to choose between being fair to himself or herself or to the Responder. Finally, as a control treatment they paired the (8, 2) allocation with itself, so that the Proposer had no choice but to offer an (8, 2) allocation.11 Subjects played all four games in different order, with no feedback following each game. The strategy method was employed so that Responders had to indicate their choices for both the reference point allocation and the alternative allocation. Figure 4.3 reports their results in terms of rejection rates for the (8, 2) allocation in favor of zero payoff for both players. The rejection rate in the game with the (5, 5) alternative is significantly higher than in all the other games, with the difference between the (2, 8) and (10, 0) games statistically significant as well. Proposer behavior anticipates these outcomes as the percentage of (8, 2) offers is 31%, 73%, and 100% against the (5, 5), (2, 8), and (10, 0) alternatives, respectively. FFF conclude that differences in rejection rates between treatments clearly indicate that intentions matter. Finally, there is an 18% rejection rate for the (8, 2) allocation when the Proposer has no choice, which FFF cite as evidence of pure income inequality aversion.12 Three-person ultimatum games, introduced by Güth and van Damme (GD; 1998), have also provided a productive framework for testing the BO and FS models. In GD

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player X proposes to split income between players X, Y, and Z. Player Y then accepts or rejects the split, with the division binding when Y accepts and all three players getting zero if the proposal is rejected. Z is a “dummy” player with the same role as player 2 in the dictator game. GD found that Proposers (player X) took advantage of Z’s dummy status, essentially dividing the money between themselves and Y, with these offers rarely rejected when Y had full information about the proposed split. Bolton and Ockenfels (1998) cite these results as strikingly consistent with their model. In the BO model, the other-regarding component of utility is evaluated relative to the social norm of equal shares for all players. Accordingly, adding a third player to the ultimatum game changes the equal division social norm from 12 to 13 , leading to a prediction of higher acceptance rates for offers in the interval [ 31 , 12 ] than in the typical two-player game. In line with the prediction, GD observed no rejections of offers in the neighborhood of 40% of the pie for Responders (player Y) when they knew the full distribution of payoffs. In contrast, such offers have a rejection rate of about 20% in a standard two-person ultimatum game (see Cooper and Dutcher 2011). Moreover, otherregarding preferences in BO depend only on own share of total payoffs. The distribution of payoffs over the other players has no impact on utility. This lines up well with GD’s observation that no rejections could be attributed to the low share allocated to the Dummy player.13 Kagel and Wolfe (KW; 2001) modified GD’s three-player design to obtain a much more demanding test of the BO and FS models. First, the responding player was randomly selected to be either Y or Z after X had made his or her allocation. This was designed to maximize the chance of the Responder getting a relatively low offer as Proposers, not knowing the identity of the player prior to making an offer, could no longer pay off the Responder at the expense of the dummy player. Second, the rejection outcome for the nonresponding player varied between treatments taking on values of $0, $1, $3, and $12, with the amount of money to be divided set at $15. Given a positive consolation prize for the dummy player, the BO model predicts that the Responder will

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Rejection rates by amount offered to responder 225 200 Number of offers

175

Acceptances Rejections

150 125 100 75 50 25 0

< $0.75 $1.00 $1.50 $2.00 $2.50 $3.00 (81%) (85%) (75%) (76%) (32%) (28%)

$3.50 $4.00 (22%) (12%)

$4.50 $5.00 > $5.24 (6%) (1%) (0%)

Offer amount (rejection rate) Figure 4.4: Rejection rates of responders.

accept any positive offer since if they reject it, they get no money and earn less than the average payoff. The FS model permits some rejections, with a positive consolation prize. However, once the level of disadvantageous inequality from rejection is greater than from acceptance, the offer must be accepted regardless of the amount of advantageous inequality the offer provides the Responder compared to the dummy player.14 As such, the $12 consolation prize treatment should effectively eliminate all rejections under the FS model as well. Pooled Responder data from KW’s treatments with positive consolation prizes are reported in Figure 4.4.15 The point prediction of the BO model is falsified because rejection rates average between 15% and 22% under the different positive consolation prize treatments. Further, with the $12 consolation prize, virtually all offers should have been accepted according to the FS model, but this treatment had the highest rejection rate of 20%. Even more damaging to both models, the rejection rate for the $0 consolation prize treatment was 21%, falling in the same range as rejection rates for the positive consolation prize treatments. Similar results were found with a negative consolation prize of $10 for the dummy player.16 In short, the consequences for the dummy player did not seem to matter to Responders.17 The invisibility of the third player in KW’s experiment calls into question FS’s and BO’s explanations of why, despite other-regarding preferences of the sort both models specify, there is typically no impact on the standard (selfish) model’s predictions in competitive markets. For both models, explaining market results such as those reported by Roth and others (1991) relies on individuals comparing their payoffs with those of all market participants. For example, FS note that the crucial factor leading to very inequitable outcomes in market games is that no single player can enforce an equitable outcome. Therefore, even very inequity-averse Responders try to turn the unavoidable inequality to their advantage by accepting low offers. However, in KW’s three-player ultimatum game, we see a relatively high percentage of Responders who get low offers turning their backs on the opportunity to reduce their income inequality relative to the dummy player by accepting a modest positive offer. A key difference between the

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0.8 0.7 Rejection rate

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$5 Rejection payoff

$10 Rejection payoff

$0 Rejection payoff

PRP TRP

0.6 05 0.4 03 02 0.1 0.0

1

2

3

4

5 >5

1

2

3 4 Offer

5 >5

1

2

3

4

5 >5

Figure 4.5: Three-player ultimatum game.

three-player ultimatum game and market games is that small payoffs can be directly attributable to a single person in the ultimatum game, whereas individual attribution is typically difficult in market games. As such, the results of KW also suggest that intentions matter, but with the added twist that “unfair” offers are rejected regardless of the consequences for “innocent” third parties. Bereby-Meyer and Niederle (BMV; 2005) report two three-person games designed to distinguish the presence of outcome-based preferences and reciprocity in bargaining games. The first class of games (called third-party rejection payoff games—TRP) is similar to the three-player game in KW with a Proposer making an offer to a Responder under each of three consolation prizes for the third dummy player—$0, $5, or $10. There are a number of procedural differences from KW as each subject plays once under each treatment with no feedback on outcomes until the session is over, and the Proposer chooses to split the money ($10) strictly between himself or herself and the Responder. In the second class of games (referred to as proposer rejection payoff games, or PRP) the Proposer is required to split the $10 between the Responder and the dummy player with no money for himself or herself. If the Responder accepts, the division is binding. If he or she rejects, both he or she and the Dummy get nothing, but the Proposer gets a rejection payoff—$0, $5, or $10—depending on the treatment. In terms of pure intention based models,18 in the PRP-$0 game, the Responder should accept all offers since the Proposer’s payoff does not depend on the Responder’s action and the dummy, not taking any action, cannot signal kindness one way or the other. In the PRP-$5 and $10 games pure intention based models allow for the possibility that low offers that would be rejected in the parallel TRP games will be accepted so as to not reward Proposers for unkind behavior. Figure 4.5 reports their results (all proposals were in dollar increments with $1 being the smallest possible allocation). In the TRP games with positive payoffs for the dummy player when offers are rejected, low offers are routinely rejected at the same, or higher, rates compared to the TRP-$0 treatment, which is inconsistent with both BO and FS models. Even more damaging, there were significantly higher rejection rates in the TRP game than in the PRP game for all payoff levels, which is inconsistent with outcomebased models that predict no difference in behavior according to players’ positions in the allocation process (Proposer, Responder, or Dummy). Pure intentionality models

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can explain why rejection rates for low offers were significantly lower in the PRP-$5 and $10 games but cannot rationalize the higher rejection rate observed in the PRP-$0 games when Responder’s payoffs were $3 or less. The results of this experiment point to multiple forces playing a role in other-regarding behavior. The data give the impression that intentions play a larger role than purely distributional concerns, but the role of pure outcome-based preferences is far from zero. Xiao and Houser (XH; 2005) also report results from a one-shot ultimatum game that are quite damaging to the FS and BO models. They add the interesting twist of Responders having the option to send written messages to Proposers, in addition to deciding whether to accept or reject offers. XH find that conditional on offers being 20% of the pie or less, rejection rates drop from 60% to 32% when Responders have the option to verbally punish Proposers—for about 80% of the low offers, a message with “negative emotions” was sent. There were no significant differences in rejection rates with and without communication for more generous offers, as well as no significant differences in the distribution of offers. XH’s results are best understood in terms of the costs of punishment. Responders have an emotional reaction to low offers and reciprocate by punishing the Proposers. When the only punishment mechanism available is the relatively costly option of rejection, they use it.19 However, as demonstrated by Andreoni and Miller (2002), otherregarding behavior is price sensitive. Given the less costly option of punishing selfish Proposers with verbal abuse, a number of Responders chose it rather than give up the money. Thus, outcome based models like the BO and FS that consider only pecuniary outcomes are likely to miss important aspects of subjects’ behavior when players have a wider array of options to consider. An important question here is the long-run implication of Responders using verbal rather than monetary punishment. In another paper, Xiao and Houser (2009) argue that monetary punishment is initially more powerful than verbal punishment. One implication of this is that if Responder’s persistently eschew monetary punishments, this would imply a long-run trend toward lower offers.20 However, there is no reason to believe that Responder’s mix of punishments will be constant over time. Additional experimental work is needed to determine the long-run equilibrium when both pecuniary and nonpecuniary punishments are available. Remark. This experiment holds lessons for field studies of other-regarding behavior. These studies typically focus on the same narrow avenues of response incorporated into laboratory experiments. But in field settings subjects usually have an array of responses available to them that are difficult to capture or quantify. Failing to identify a reciprocal response along one avenue doesn’t mean that a reciprocal response hasn’t occurred, nor does it imply that reciprocity isn’t playing an important role in driving individual’s choices. As such, one needs to be particularly careful when drawing conclusions from less structured field settings. Summary. The BO and FS outcome-based models of social preferences pulled together a surprisingly large number of experimental outcomes and organized them using other-regarding preferences based on income inequality. As such, they provided a clear focal point for further experimental work. Although subsequent experiments have been hard on both models, these papers made (and continue to have) a major impact on the literature and have moved the discussion forward in terms of helping to identify exactly what kind of fairness considerations underlie deviations from the standard selfish, income-maximizing model. At this point the data suggest: (1) outcomes do matter, to some extent at least, as—for example—when Responders reject unequal offers

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in cases where Proposers have no choice but to make such offers, and (2) intentions matter as well, possibly even more than outcomes. There still remain important methodological issues to be addressed in this literature. Reading through all these papers at once, we are struck by the varying methods used by different researchers. Strict comparisons across papers are, therefore, difficult, and it is unknown how many of the results reported in the literature are robust to changes in methodology. As a vivid example of this problem, consider the following question: why do subjects in FFF reject unequal offers when Proposers have no choice but to make such offers? Difference aversion is an obvious explanation for this, but results from Charness and Rabin (CR; 2002) force us to question this. In a dictator game, CR ask player Bs to choose between (800, 200)—200 being B’s payoff and 800 being A’s payoff—versus a (0, 0) allocation and find that 100% of the 36 subjects queried chose the (800, 200) option. It is hard to argue that the differing results of FFF and CR are anything other than an artifact of how preferences are being elicited. One possible methodological cause is CR’s use of an “equal-opportunity” procedure, whereby each subject got to choose as a B player knowing that his or her actual position as the A or B player would be determined randomly at the end of the session; other researchers have found that equal-opportunity procedures reduce inequality aversion (Bolton and Ockenfels 2006). Another possibility is that subjects don’t fully understand that the Proposer’s choice is irrelevant in FFF but would understand this if they gained experience via repeated trials with feedback. The point is that further work is needed to know how researchers’ differing methodological choices are affecting the observed behavior and, by extension, conclusions reached with respect to other-regarding preferences.21 The question of whether to use one-shot experiments (or repeated trials without feedback) versus repeated trials with feedback comes up repeatedly in this literature. The argument for using one-shot experiments is that these are particularly clean— there is no possibility of unwanted repeated game effects and, because there is no rematching of subjects, games from the same session can be treated as fully independent observations.22 However, the decision to not allow for learning via experience can affect results. For example, if one looks at a standard ultimatum game played for ten rounds, the distribution of proposals is typically much more dispersed in early compared to later rounds, with the frequently stated stylized result of a high concentration of offers in the 40% to 50% range (and minimal rejection rates for such offers) emerging only in later rounds (see, for example, the data reported in Roth et al., 1991). Economists have traditionally preferred experiments with repeated trials and feedback in response to the original Wallis and Friedman (1942) critique of economic experiments: It is questionable whether a subject in so artificial an experimental situation could know what he would make in an economic situation; not knowing, it is almost inevitable that he would, in entire good faith, systematize his answers in such a way as to produce plausible but spurious results. For a satisfactory experiment it is essential that the subject give actual reactions to actual stimuli. . . . Questionnaire or other devices based on conjectural responses to hypothetical stimuli do not satisfy this requirement. The responses are valueless because the subject cannot know how he would react.

This is not to say that repeated trials are the only way to conduct experiments, but more investigation is needed about whether results based on one-shot experiments,

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or experiments without feedback, yield results that are robust to subjects gaining experience. Another methodological question that comes up frequently in this literature is whether to use the standard direct-response method or the strategy method. The appeal of the strategy method is obvious, as it allows more data to be gathered per subject, but once again the question comes up of whether this affects behavior. Results vary as to whether the strategy method leads to different results than direct response.23 At the very least, it seems clear that it can matter. Brandts and Charness (2003) and Brosig, Weimann, and Yang (2003) both find that punishment rates for an unkind and/or deceptive act are significantly lower when the strategy method is used. Along similar lines, Casari and Cason (2009) find significantly less trustworthy behavior in trust games when the strategy method is used. The size of the effect can be large. In Brandts and Charness, the clearest example of an unkind act occurs when a player lies about his or her intent to make a fair choice. Using direct responses, this sort of lying is punished in 56% of the observations (9/16), but the punishment rate is halved to 28% (19/69) when the strategy method is used. Casari and Cason observe that 40% of subjects (14/35) return nothing when the direct response method is used, but this jumps to 60% (43/72) when the strategy method is used. In contrast to the preceding, there are also cases where the strategy method does not matter, as in the examples reported by Brandts and Charness (2000). When an effect exists, the strategy method yields less reciprocal behavior than direct responses. This suggests an anchoring and adjustment process in line with other examples of framing effects—when subjects are faced with a problem that has multiple dimensions, the framing can impact which dimension gets the most attention and which is treated as a secondary concern.24 In the environments discussed before, subjects are trading off reciprocity for kind/unkind actions against payoff maximization. Direct responses seem to focus attention more on reciprocity, yielding more reciprocal behavior. From a practical point of view, the issue is that otherregarding behavior can be sensitive to the method of elicitation. This makes it difficult to directly compare studies that have used different elicitation methods. C Social Preferences versus Difference Aversion At this point in time it seems safe to state that deviations from the predictions of the standard selfish model cannot be explained solely based out outcomes, as reciprocity and intentions play an important role. Nonetheless, outcome-based preferences still seem likely to explain some portion of other-regarding behavior. Within the BO and FS models, difference aversion is the driving force behind these outcome-based preferences. Beginning with Charness and Rabin (2002) and continuing with Engelmann and Strobel (ES; 2004), it has been argued that social welfare preferences—concerns for efficiency (defined as maximizing total payoffs for the group) and the payoffs for the least-well-off players in the group (maximin preferences)—are the key factors underlying outcome based preferences rather than difference aversion. Both of these papers report a number of results supporting this position. For example, consider player 2 choosing over distributions A, B, and C in cases X and Y shown in the table below (drawn from ES). For X, player 2’s payoff is independent of their choice. Alternative A is efficient, maximizing total payoffs. It is also a maximin allocation because it has the highest payoff for the least-well-off player. In contrast, B maximizes player 2’s utility according to the BO model, with C maximizing player 2’s utility according to FS.25 Alternative A is overwhelmingly the most popular choice.

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Allocation Player 1 Player 2 Player 3 Totala Percentageb Notes:

a

A 16 8 5 29 70.0

Choice X B 13 8 3 24 26.7

C 10 8 1 19 3.3

A 16 7 5 28 76.7

Choice Y B 13 8 3 24 13.3

C 10 9 1 18 10.0

Sum of players’ payoffs. b Frequency with which the allocations were chosen in ES (2004).

The allocations in choice Y are the same as X, with the exception that in Y it costs player 2 a modest amount of money to choose the efficient, as well as the maximin, outcome. BO now predicts choice of B or C, with FS still predicting C.26 In practice, this small increase in cost has little impact on the strong tendency to choose the efficient (as well as maximin) allocation. Looking at a variety of choices of this sort, both CR and ES estimate the relative impact of efficiency considerations, maximin preferences, and difference aversion of the sort specified in BO and FS on choices, concluding that social welfare preferences play a more important role than difference aversion. Earlier results by Kagel, Kim, and Moser (1996) cast doubt on this conclusion. Kagel and others report an ultimatum game experiment with asymmetric information and asymmetric payoffs that shows players’ concerns for efficiency are trumped by own income concerns when the two are in strong conflict. In a treatment in which the proposer has a 3-to-1 conversion ratio from chips to dollars, with only Proposers knowing the conversion ratio, and bargaining is in terms of chips, Proposers offer Responders slightly less than half the chips on average, with only 8% of their proposals being rejected.27 However, when payoffs favored Responders 3 to 1, again with only Proposers knowing the conversion ratio, mean offers averaged 31.4 chips overall, as Proposers “concern for efficiency” vanished in favor of own income, in spite of rejection rates averaging some 21% of all offers. Responding to ES, Bolton and Ockenfels (2006) argue that the essential question is the willingness to pay for efficiency as opposed to equity. They provide results from an experiment in which twice as many subjects deviate from higher own payoffs in favor of the more equitable outcome as opposed to deviating in favor of the more efficient outcome. In response Engelmann and Strobel (2006) point out that it is difficult to identify the correct metric for measuring the trade-off between efficiency and equity, noting that in BO’s experiment subjects are asked to pay a lot for relatively small percentage increases in efficiency. Fehr, Naef, and Schmidt’s (2006) response to ES is to identify strong subject-population effects in the degree with which subjects favor efficiency over equity. They replicate one of ES’s choices, reporting that 53% of noneconomists prefer the most egalitarian (and least efficient) allocation, as opposed to 30% when the subjects are economics and business students. They attribute the stronger preference for efficiency over equity in ES’s experiment as opposed to other studies to the fact that ES’s subject population consisted of economics and business majors. Reviewing this exchange of views, the literature suffers from attempts to oversimplify subjects’ behavior. There is great heterogeneity among subjects’ preferences, as Fehr, Naef, and Schmidt (2006) convincingly demonstrate, and subjects appear to be able to make reasonable adjustments in how much they rely on any one criterion depending on the costs and benefits involved. Further, reciprocity/intentionality appears to be a stronger force in driving subjects’ choices than any purely distributional concerns. For example, only 18% of Responders rejected the (8, 2) offer in FFF when Proposers have

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no choice, but 45% of such offers are rejected when the Proposer could have offered a fair split (5, 5). D Models Incorporating Reciprocity/Intentions of Proposers The experimental literature responding to introduction of the FS and BO models made it clear that a full theory of other-regarding preferences must account for more than inequality aversion. Limiting attention to distributional issues, the sources of otherregarding behavior clearly extend beyond inequality aversion, given consistent evidence of preferences for social welfare and Rawlsian (maxmin) preferences. A good model should be flexible enough to capture these diverse motivations. There are also a number of factors driving other-regarding behavior beyond distributional preferences that a good model should incorporate. To be overly simplistic, the golden rule of human behavior often seems to be “do unto others as they have done unto to you.” In other words, individuals should place positive weight on the payoffs of others who have treated them kindly and negative weight on the payoffs of unkind individuals. This apparently straightforward formulation immediately raises the critical issue of how to define kind/unkind actions. The experimental evidence suggests that a number of factors may play into this definition. How you perceive an action that could potentially be interpreted as being unkind is likely to depend on the specifics of the situation. What other options were available (menu dependence)? Did the other person act intentionally or were you harmed by accident (intentionality)? Did the other person harm you because they anticipated you trying to harm them (second-order beliefs)? Was the other person’s action any worse than what would normally be expected (social norms)? An ideal formal model of reciprocity would capture all these aspects of kindness, but this is a Herculean task given the diversity of issues involved. This has not, however, stopped a number of authors from making the attempt. The model of Charness and Rabin (2002), the most influential successor to BO and FS, introduces a simple model that allows both for a wide variety of distributional preferences as well as reciprocity. The functional form is shown in equation (3). The variables ρ, σ , and θ are parameters, r and s are indicators for x j > xi and xi > x j , respectively, and q = −1 if the other player has “misbehaved” and equals 0 otherwise. Note that the utility function gives j ’s utility, corresponding to the notion that the utility of a Responder is being measured u j (xi , x j ) = (ρ · r + σ · S + θ · q) xi + (1 − ρ · r − σ · s − θ · q)x j

(3)

Ignoring reciprocity, this functional form nests a number of concepts about otherregarding preferences, such as competitive preferences, difference aversion, and social welfare. By fitting the parameters of the model from experimental data, it is possible, in principle, to sort out what elements of other-regarding preferences best explain behavior, with CR’s experimental work including an exercise of this sort. Misspecification of the model, as well as heterogeneity between subjects, makes econometrically distinguishing between different types of other-regarding preferences an extremely difficult task in practice. That said, the CR model provides a richer framework for thinking about distributional preferences than BO or FS. The role of reciprocity in the CR model lacks a solid theoretical foundation—the weight on another player’s payoff is reduced if they have “misbehaved.” The definition of misbehavior is somewhat vague, but we view this as a useful simplification.28 While other theories of reciprocity are undoubtedly more elegant, we are primarily interested in models of reciprocity as a tool for interpreting experimental data.29 Misbehavior is

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a little like pornography—we can’t easily define it, but we know it when we see it. The appendix to CR includes a more sophisticated version of the theory in which unkind behavior is endogenously defined. This appendix is essential reading for anybody who wants to truly understand their theory. Many theories that model reciprocity follow Rabin’s (1993) lead in relying on the mechanics of psychological game theory, implicitly for CR (in the appendix) and explicitly for Dufwenberg and Kirchsteiger (2004) and Falk and Fischbacher (2006). There are good reasons for taking this approach. Good or bad behavior can often be defined only in relationship to what situation the actors believed they faced. For instance, consider defection in a prisoner’s dilemma. This is an unkind act if cooperation is expected by the other player, but most people would agree that defection is perfectly reasonable if the other player is expected to defect. Beliefs must play a critical role in any theory that attempts to capture this aspect of reciprocity. That said, there are important aspects of reciprocity (or, to be more precise, kindness) that are not captured well in models based on psychological game theory (i.e., Rabin 1993; Dufwenberg and Kirchsteiger 2004; Falk and Fischbacher 2006). In many cases the beliefs that are relevant are not first- or second-order beliefs about what the players will do, but rather beliefs about what a “normal” person would do. If I leave a 10% tip following good service at a restaurant in the United States, I am cheap and the waiter’s anger is reasonable. In most European countries this would be kind behavior, and the waiter should probably be grateful. At least some of the models of reciprocity based on psychological game theory implicitly recognize that norms matter, but the source of norms is generally not modeled explicitly. For example, the full model for Charness and Rabin compares a player’s behavior with λ∗ , defined as “the weight they feel a decent person should put on social welfare.” This parameter serves the purpose of a social norm and is exogenous to the model. Hopefully, future work will make more progress in making reference points based on norms, such as λ∗ , endogenous. Psychological game-theoretic models of reciprocity undoubtedly provide sophisticated theories of a complex phenomenon, but our concern here is less with elegance than with useful tools for understanding experimental data. Theories based on psychological game theory fall short of this goal on two counts. First, as noted in our discussion of Rabin (1993), these models are not terribly tractable and often yield implausible equilibria. The reliance on beliefs, while clearly an important benefit of these models, also creates problems. Distributions of outcomes can be observed directly, but beliefs are not so easily accessible to researchers. Charness and Dufwenberg (CD; 2006) provide a useful demonstration both of the importance of beliefs and how an experimental design can directly capture the interaction between beliefs and other-regarding behavior. They study a version of the trust game in which the second player (as a treatment variable) can send a preplay message to the first player. This gives the second player the opportunity to make nonbinding promises about how much they will return (“roll” in the version of the game studied by CD). In keeping with many previous results in the experimental literature, CD find that cooperation increases with preplay communication. The novel part of the paper is its focus on beliefs. CD develop a theory incorporating guilt aversion, positing that players don’t like to harm others relative to their beliefs.30 In terms of the trust game, the second player experiences disutility if he does not return money and believes that the first player expected money to be returned. Promises serve as a form of precommitment in this framework. If a second player believes his or her promise affects the expectations of the first player, that player experiences greater disutility from failing to return money.

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Thus, the theory predicts not just an effect of promises on actions but also an effect on beliefs. CD test this prediction by using an incentivized mechanism to gather beliefs and second order beliefs. Following promises, beliefs shift in the predicted direction. This is not direct evidence that the shift in beliefs is causing the shift in behavior, an issue that has been studied extensively in the subsequent literature but is certainly consistent with the theory.31 For our purposes, we are more interested in CD’s methods than the theory of guilt aversion. CD provide an important guidepost for how experimenters interested in other-regarding behavior can directly address the issue of beliefs. E Other-Regarding Behavior and Utility Maximization Much of the existing literature on other-regarding behavior revolves around attempts to identify the preferences underlying seemingly anomalous behavior. As such, it can be characterized as neoclassical economics flavored with a dash of psychology. Subjects are presumed to be maximizing a stable utility function, with the theory departing from standard microeconomics only through the arguments in the utility function. Even theories that have roots in psychological game theory (e.g., Charness and Rabin 2002) rely on subjects maximizing utility subject to stable preferences. The work described in this section directly addresses the question of whether or not other-regarding behavior is consistent with rational choice theory as understood by economists. Andreoni and Miller (AM; 2002) address this question in the most direct possible fashion and provide a strong affirmative answer. Subjects made decisions in a series of modified dictator games. Both the available budget and the relative price of giving were varied across games. In other words, subjects were asked to choose between payoffs for themselves and payoffs for another anonymous subject under a variety of budget constraints. Rather than testing any particular theory of other-regarding preferences, AM focus on whether choices are consistent with the generalized axiom of revealed preference.32 They find that a remarkable 90% of the subjects have no violations of GARP (with at least eight choices per subject), implying that most subjects’ choices are consistent with maximization of a quasi-concave utility function. The 23% of subjects who never gave away any money trivially have no violations of GARP, but most of the subjects who gave money away also make choices that are compatible with a rational choice model in terms of satisfying GARP. AM note that there is a great deal of heterogeneity among subjects—beyond the large number of subjects (47%) whose behavior is most consistent with selfish behavior, there were sizable numbers of subjects whose choices are most consistent with Leontief preferences (30%), splitting the money equally between themselves and the other player, or treating own and others’ payoffs as perfect substitutes (22%) by giving all the money to the player with the highest payoff.33 This heterogeneity needs to be taken into account when looking at otherregarding behavior. Finally, AM present evidence that behavior reported in other otherregarding experiments could have been (approximately) generated by the distribution of preferences they report. They argue that this is evidence that preferences are robust over a variety of settings. Fisman, Kariv, and Markovits (FKM; 2007) provide a more powerful test of GARP as subjects are asked to make fifty decisions rather than the eight used in most of AM’s sessions. Looking at decisions in two-person modified dictator games of the sort AM employ, varying the budget and price of giving, the proportion of subjects whose decisions are completely consistent with GARP falls to 11%. This decline relative to AM’s data is to be expected given the substantial increase in the number

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of decisions. However, FKM conclude that violations of rationality are generally small because 86% of subjects have CCEI scores, which measure how much a subject’s budget constraint would need to be perturbed to make their choices consistent with GARP (Afriat 1972), of 0.8 or greater.34 FKM also expand AM’s analysis of individual utility functions by studying three-person dictator games, so that they can address broader classes of other-regarding preferences. While they continue to find evidence in favor of social welfare preferences, their primary conclusion is that preferences are quite heterogeneous.35 The results of AM and FKM make a good case for other-regarding choices being consistent with maximization of a well-behaved utility function. Both show that preferences are reasonably consistent with standard theory in stable environments in that other-regarding behavior is price sensitive in the usual ways. Further, there is a good deal of heterogeneity in the preferences, with large numbers of subjects having standard selfish preferences and others having other-regarding preferences. Both studies rely on environments that, other than changing prices and budgets, are stable. This misses some of the key problems already identified in terms of standard utility functions: altering seemingly irrelevant features of the decision-making environment that often change choices (see Section III.C) or when the situation is sufficiently nontrivial that learning is involved (see Cooper and Stockman (2002) in Section II.F). F Learning The literature on other-regarding preferences largely takes as given that the observed differences from classical game theory result from nonstandard preferences, with the debate centered around what form these preferences take. The results of AM and FKM provide support for this approach. However, models of bounded rationality and learning can provide an alternative explanation for at least some of the anomalous behavior relative to standard (selfish) preferences, while still maintaining the standard selfish-preference model. Although it seems unlikely that models of bounded rationality and learning can entirely explain the wide variety of other-regarding behavior observed in the laboratory, these models provide a good explanation for a considerable number of outcomes at odds with the standard selfish preference model. Bounded rationality and learning first entered the other-regarding behavior literature in a pair of articles, Roth and Erev (RE; 1995) and Gale, Binmore, and Samuelson (GBS; 1995). Although the models used in these papers differ, the main point is roughly the same: suppose players in the ultimatum game have completely standard selfish preferences but are adaptive learners. Rather than maximizing payoffs, players have an initial distribution over their available strategies (with the source of this initial distribution not explained). Over time, strategies that earn higher payoffs are played with greater frequency. Play in a learning model of this sort does not necessarily converge to the subgame perfect equilibrium. The logic of subgame perfection relies on players making logical inferences about play off the equilibrium path, but adaptive learning depends solely on outcomes players actually observe. If an action is taken only rarely, players never learn what payoffs would have resulted from this action and can therefore persistently play a suboptimal strategy off the (Nash) equilibrium path. In both models, this is precisely the mechanism that leads to a prediction that the ultimatum game need not converge to the subgame perfect equilibrium. Reaching the subgame perfect equilibrium under an adaptive learning model is a two-step process: Responders must learn to stop rejecting low offers and then Proposers must learn that low offers will be accepted and hence are highly profitable. The timing

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here is tricky as Responders must stop rejecting lower offers before Proposers have stopped making them. However, the disparity in incentives between Proposers and Responders makes this highly unlikely. Rejecting a low offer costs a Responder little, but having a low offer rejected is quite costly given that roughly equal splits are almost always accepted. Proposers therefore learn to stop making low offers faster than Responders learn to accept them, so that play fails to converge to the subgame perfect equilibrium. This contrasts with games like the best-shot and the market game, where strong out-of-equilibrium incentives push the learning process toward the subgame perfect equilibrium (which has highly asymmetric payoffs in both cases) matching the strong convergence actually observed in these games.36 Experimenters responded to these two learning papers by largely ignoring them. This was in part due to holes in the theory. Both RE and GBS make the point that behavior in the ultimatum game can be explained without resorting to other-regarding preferences. This is not quite the same thing as showing that other-regarding preferences are not playing a role, and indeed it seems unlikely that other-regarding preferences don’t matter. Both theories are also incomplete since behavior depends critically on the initial distribution of strategies, which is determined exogenously. A clever experimental design by Abbink and others (2001) reveals serious flaws with this approach. They consider mini-ultimatum games where the payoff to the proposer following rejection of an uneven split is a random variable. The value of this variable is drawn at the beginning of each session and remains fixed throughout the session. The proposers’ payoff following rejection is shown to Responders but not Proposers, who know only the distribution of values. Responders’ behavior varies with the realization of the Proposer’s punishment payoff, an effect that the learning models cannot predict. The learning models do a poor job of tracking the data if the initial distributions of strategies are forced to be identical across treatments (and don’t do so wonderfully even when these are allowed to vary). Abbink and others make it clear that adaptive learning cannot provide the entire explanation for other-regarding behavior. Another serious problem was a lack of supporting experimental evidence. The theories proposed by RE and GBS assume Proposers and Responders learn in an identical fashion. Learning by Responders is predicted to be slower than Proposers’ learning, but this is solely due to lower incentives to learn rather than any inherent difference between the two. Both models therefore predict that Responders’ behavior should change with experience, albeit slowly. This critical prediction is difficult to test given the small changes predicted and the limited number of plays of the game in most experiments, so that power becomes a serious problem. The result is that most studies show some learning on the part of Proposers, but changes in the behavior of Responders are generally too small to be statistically significant (see Slonim and Roth 1998, for example). However, two papers that are specifically designed to provide more powerful tests of Responder learning find evidence for it.37 List and Cherry (LC; 2000) run a variant of SR’s high-stakes experiment, where Proposers earn the right to propose rather than having it determined exogenously. This results in substantially more low offers than is typical—28% of offers are less than a quarter of the pie. With an enlarged sample of low offers, LC find that (controlling for the size of offers) rejection rates fall with experience. Although this effect is in line with the predictions of the RE and GBS model, it does not represent unqualified support for these models since most of the decline observed in LC occurs in the last few periods, which is more consistent with a reputation model than an adaptive learning model. Cooper and others (CFRZ; 2003) manipulate the experience received by Responders by doubling the number of Proposers relative to Responders.38 Since Responders are

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playing twice as often as Proposers, this tends to equalize the speed of learning between Proposers and Responders. In the standard setup, relatively fast learning by Proposers drives the predictions of RE and GBS that low offers will continue to be rejected with experience. This prediction should be weakened in the 2 × 1 treatment. Indeed, CFRZ find that rejection rates are lower in the 2 × 1 treatment than in controls that have an even number of Proposers and Responders. They also find that a history of receiving low offers makes subjects more likely to accept low offers and that the treatment effect does not widen over time, consistent with learning slowing over time. Although these results are consistent with adaptive learning, the evidence is indirect as the treatment effect cannot be observed with the naked eye, and the magnitude of the estimated effects is moderate. To directly test the prediction that rejection rates fall with experience in the ultimatum game, Cooper and Dutcher (CD; 2011) pool data gathered in seven different experiments.39 Their criteria for choosing studies for this meta-analysis was as follows: data had to be from “standard” ultimatum games (i.e. played with direct response rather than the strategy method, random re-matching between rounds, random selection into roles, endowments are provided exogenously, Proposers and Responders play with equal frequency) and subjects had to play at least ten rounds. The main result of this meta-study can be seen in Figure 4.6. The x-axis gives the proportion of the pie offered to the Responder and the bars show acceptance rates. The labels at the top of the bars show the frequency of each offer category. Since only 3 of the 6 data sets have more than 10 rounds, this figure compares data from rounds 1–5 with data from rounds 6–10. The overall pattern is clear. The acceptance rate rises with experience for relatively large offers but falls for small offers (20% of the pie or less). The magnitude of these changes is small, but the advantage of doing a meta-study is that the large data set provides the necessary power to detect small changes. CD run appropriate regressions using the entire data set, controlling for session and individual effects, and confirm that the changes in acceptance rates with experience, increasing for relatively large offers and decreasing for small offers, are significant at the 1% level. The regressions also indicate that there is no learning beyond the first ten periods, consistent with the learning models’ prediction that learning should slow down with experience. CD establishes beyond a reasonable doubt that Responder behavior in the ultimatum game changes with experience. The aggregate effect is small, but that is predicted: what is not consistent with the learning models of RE and GBS is the reduced acceptance rates for the very lowest offers shown in Figure 4.6. This suggests that the adjustments observed in behavior over time reflect something beyond simply learning to follow the money-maximizing strategy of accepting all offers. CD note that this pattern is consistent with learning in a model that extends Charness-Rabin’s framework by explicitly allowing Responders’ perceptions of kindness to depend on their belief about the distribution of offers. As Responders learn about the distribution of offers, their beliefs—and hence their actions—should change. CD present evidence based on individual subject data that is consistent with such a model.40 That is, while learning is subtle at the aggregate level, it is quite powerful at the individual level. If subjects need to learn a norm about what is an acceptable offer and are, on average, correctly calibrated to begin with, this is precisely the pattern that should be observed. While observed changes in behavior are small for Responders in the ultimatum game, changes in behavior can be quite large in other, related, situations. For example, Cooper and Stockman (CS; 2002) study a three-player sequential step-level public goods game. Players take turns deciding to contribute or not contribute to a public good. The good is

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r C > A, and voter 3 has preferences C > A > B. This results in a majority-rule cycle, with A >m B >m C >m A, where >m denotes the strict majority binary relation. The existence of such a cycle implies that sophisticated voting will lead to different outcomes than “naive” voting in a two-stage agenda. Consider the sequential binary agenda, ( A, B, C ), where in the first stage A is voted against B and in the second stage the winner of the first stage is voted against C . Then, working from the end, the last stage outcome will be B if B is the firstround winner and C if A is the first-round winner. Therefore, with sophisticated voting, the vote in the first round is treated as, in effect, a vote between B and C rather than the literal vote between A and C . Thus, voter 1 will vote for B in the first stage, even though his or her naive or myopic preference is to vote for A. For the other two voters, their myopic and sophisticated voting strategies coincide. Thus, the sophisticated outcome here is B, while the outcome would be C if everyone voted myopically. Like finite alternating offer bargaining and other simple extensive form games in economics, agenda-setting games are natural candidates for studying behavioral issues of subgame perfection, dominance solvability, strategic sophistication, and equilibrium. Also like bargaining games, the theoretical results have shaped the way scholars in the field approach applied questions (such as agenda influence in the legislatures), and, therefore, careful testing of the theory of sophisticated voting over binary agendas has the potential for significant impact. The initial experiments related to sophisticated voting are reported in Levine and Plott (1977), Plott and Levine (1978), and Cohen, Levine, and Plott (1978) and used much more complicated agendas than the simple example given before. While the agendas they explore are more general than the binary amendment procedure, the basic ideas of backward induction, dominance, and sophisticated voting can be applied directly because every vote involves a binary choice between subsets of feasible alternatives, and the agendas are determinate in the sense that the terminal nodes of the voting tree are all associated with unique feasible outcomes. There is one important difference in these early experiments: voters had information only about their own preferences over the alternatives, so these were games of incomplete information. However, extensive discussion was an important component of the committee decision-making procedures, and voters had an opportunity to communicate their preferences to other voters. Thus, while perhaps dubious as an equilibrium prediction for these environments, the sophisticated voting outcome is a natural benchmark. Here is an example of the kind of agenda they consider, which one might call a divide-the-question agenda. Suppose three economists are trying to decide to which restaurant to go, and there are four possibilities: one is expensive and serves Italian food (EI), one is cheap and serves American food (CA), one is cheap and serves Italian food (CI), and the fourth is expensive and serves American food (EA). The restaurants differ along two different dimensions, and one can consider “dividing the question” by voting first on one dimension (E vs. C) and next on the second dimension (A vs. I). This is equivalent to a two-stage agenda where the first vote is between the sets {E I, E A} and {C I, C A} and the second stage is a vote between the two alternatives of the pair that won in the first round. Note that this is not equivalent to

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Agenda Item 2a A Item 1 A A

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Figure 6.4: Sample agenda. Source: Plott and Levine (1978).

a binary amendment procedure. For example, a binary amendment procedure with the alternatives ordered {E I, E A, C I, C A} would imply a three-stage agenda, where (in set notation), the first vote is between {E I, C I, C A} and {E A, C I, C A}, and so forth. In all agendas considered in these three papers, all players have strict preferences, and there is an odd number of voters, so if one analyzes the games as if the players had complete information about ordinal preferences over the alternative set, then the games are dominance solvable by the Farquharson-Niemi-McKelvey sophisticated voting algorithm. The experiments were conducted with two RAs in the room, one to chair the discussion and another to record the proceedings. Discussion was limited in several ways: promises of side payments were not allowed; threats were not permitted; subjects could only make qualitative statements about their preferences, not quantitative statements about their exact payoffs from different alternatives; and straw votes “down the agenda” were not permitted. There were twenty-one different voters in the committee, which had to decide which one of five possible alternatives, {A, B, C, D, E }, to select via a majority-rule agenda. The preference orders of the twenty-one voters implied a majority rule relation in which A was a Condorcet winner, E was a Condorcet loser,32 and the middle three alternatives cycled: B >m C >m D >m B. They conduct a number of three-stage agendas, an example of which is shown in Figure 6.4. Under sophisticated voting, A should be the outcome in all agendas. In the agenda illustrated in Figure 6.4, for example, the first stage is a vote between { A, B} and {C, D, E }. If the outcome is {A, B}, then a final vote is conducted between A and B. If the outcome is {C, D, E }, then a vote is conducted between {D, E } and {C }, with a final third stage needed only if the outcome of the second stage is {D, E }. Working from the last stage back to the beginning of the agenda, it is easy to see that the sophisticated equivalent of {D, E } is D, and hence the sophisticated equivalent of {C, D, E } is C . The sophisticated equivalent of { A, B} is A. Therefore {A, B} defeats {C, D, E } in the first stage under sophisticated voting; then A defeats B in the second stage. The other agendas in the paper are solved by similar logic.

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The design of the experiments and the analysis of the data was not motivated by a desire to test the Farquharson-McKelvey-Niemi theory of rational sophisticated voting.33 Indeed the game-theoretic predictions are barely alluded to in the paper. Instead they propose a mixture of types model where there are three different possible behavioral decision rules. The first decision rule is called sincere voting. Because sincere voting is not well defined over subsets, they define it as simply voting between the top (i.e., most preferred) elements of the two subsets. Hence this decision rule can be thought of as “optimistic,” or hope-for-the-best, behavior. The second decision rule is the exact opposite, where players behave pessimistically; it is called the avoid-theworst decision rule. In this case a voter would compare the least preferred alternative from each subset and vote for whichever set has the better worst alternative. The third decision rule strikes a balance between the optimistic and pessimistic rules and is called the average-value decision rule. In this case, the individual evaluates each subset, in terms of the expected utility of a uniformly distributed lottery over the alternatives in the subset and votes for the subset with the highest expected utility under this assumption. Thus, unlike the first two decision rules, the average-value decision rule depends on more than just the ordinal ranking of the (pure) alternatives. Individuals are then considered to be random variables with respect to following one of these three decision rules, and the theory is fleshed out with a number of parameters governing the relative frequency of these decision rules in the subject population. The authors first conducted several pilot studies that are not reported in the paper. The main value of the pilot studies, in addition to fine-tuning the instructions and procedures, is that the data from those studies could be used to estimate the parameters of their decision rule model. Using these parameters, they design the agendas used in the experiment reported in the paper (series 4 data). In most of these agendas, the sophisticated outcome was different from the predicted outcome based on their model. Except for only one agenda, their model was generally successful. In the single agenda where the model failed to correctly predict the outcome, the outcome achieved by the committee was the sophisticated outcome (and the Condorcet winner).34 That committee was the only committee that was allowed to conduct a down-the-agenda straw vote, which essentially converted the agenda voting game to one of complete information. These results are not easy to interpret. Clearly they are not a rejection of sophisticated voting theory, which either implicitly or explicitly requires complete information (or nearly complete information) in order for the dominance solvability argument to make any sense. In these experiments, voters had only private information about their own preferences and were not even given probabilistic information about other members’ preferences. It is really an environment with decision making under conditions of (nearly) complete ignorance. Thus it is not surprising that the data can be mostly explained in terms of theories of decision making under ignorance, such as the principles of insufficient reason (decision rule 3) or maximin (decision rule 2). The allowance for discussion was apparently insufficient to produce meaningful information transmission, with the one exception arising when the discussion was allowed to include straw votes. The Levine-Plott (1977) paper reports a similar exercise in predicting agenda outcomes from a field application of the agenda model. The authors belonged to a flying club that was deciding on the composition of a new fleet of planes. There were many possible options, and the authors were asked by the club to devise an orderly voting procedure to produce an outcome. The authors obtained rough preference information

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from the other members via discussion at earlier meetings and personal knowledge of the other members35 and then applied their model to construct an agenda designed to produce one particular outcome.36 Indeed, the agenda did succeed in producing the targeted outcome, even though one of the other options was a Condorcet winner. Cohen, Levine, and Plott (1978) report the results of some further series of divide-thequestion agenda experiments and results that are mostly in line with the findings of Levine and Plott (1977) and Plott and Levine (1978). There have been only three subsequent experiments to study sophisticated voting with fixed binary agendas. Herzberg and Wilson (1988) note that the lack of support for sophisticated voting in the earlier studies was probably at least partly due to the difficulty or impossibility of calculating optimal sophisticated strategies because preferences were not common knowledge. Besides this, even if preferences were common knowledge, the strategies used by other voters may be difficult to predict as well. Furthermore, all these difficulties would presumably be even more difficult in longer agendas. In an attempt to create a laboratory environment that minimized these informational complexities, they consider small five-voter committees, in which only one of the voters is a human subject. The remaining voters are computerized and subjects are provided with sufficient information to infer exactly how the computers will vote at each stage of the agenda.37 There are two main findings. First, the hypothesized relationship between agenda complexity (measured by agenda length and number of feasible alternatives) finds little support in the data. The six-alternative agenda has the highest frequency of sophisticated outcomes. More supportive of this hypothesis is the finding that longer agendas produce more “stray” outcomes (i.e., neither sophisticated voting outcomes nor sincere voting outcomes). Second, sincere voting outcomes occur more frequently than sophisticated voting outcomes in all three agendas. The agendas are all fairly long, as there are either four, six, or eight alternatives and the agendas are, respectively, three, five, and seven stages long. Like the agenda experiments described earlier, subjects are naive and inexperienced, vote over only one of the agendas, and play that game exactly once.38 The paper leaves open a number of questions about both design (e.g., the use of sincere computerized voters and inexperienced human voters) and substance (e.g., how voters formulate their voting strategies in an agenda under conditions of complete information). Regarding the latter, there are many findings from bargaining games39 and other multistage games40 where players have to make multiple sequential decisions and do not follow backward-induction solutions. This is true even in cases where the backward induction solution is efficient and perfectly equitable (Fey, McKelvey, and Palfrey 1996), although with repetition there is convergence in the direction of the backward-induction solution.41 There is also a concern about the use of computerized subjects and the possibility that telling subjects the computers vote sincerely may lead subjects to adopt a similar rule of thumb. Eckel and Holt (1989) take a somewhat different avenue to extend these earlier findings. In particular, they choose to look at extremely simple two-stage agendas and run different treatments that combine and extend some of the features of the Plott and others’ and Herzberg-Wilson studies. First, they run sessions both with complete preference information and with private information. Second, they repeat the task for the subjects ten times. They have a second treatment concerning how often the preference assignments were changed during the ten rounds. In one case (call it random), they are changed every round, and in the other case (call it fixed), they

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remain unchanged until the sophisticated voting outcome is achieved, at which point they change. In the latter case, subjects are not informed about the rule for changing assignments. For the private-information treatments, partial leakage of this private information can take place in two ways: a restricted form of prevote discussion similar to the Plott and others’ procedures is allowed; through task repetition voters have an opportunity to learn how to forecast voting behavior in the second stage of the agenda.42 In all their sessions, there were three alternatives, {A, B, C }, and three preference types, A > C > B, C > B > A, and B > A > C , so the preference profile produced a majority-rule cycle. There were nine subjects and three of each preference type, and eight sessions were conducted. The two-stage agenda was always first to vote between alternatives A and C and second to vote the winner of the first stage against B. The only difference between sophisticated and sincere voting arises in the first round, where the three A > C > B voters should vote for C because B will defeat A in the second round (6 to 3), but C defeats B. A clever aspect of their design is that all three of the Plott and others’ decision rules (sincere, avoid-the-worst, and average-value) predict sincere voting by all types at both stages. This provides a very clean test of the decisiontype mixture model, against a clear alternative hypothesis: sophisticated voting. There are three main findings. First, repetition is necessary and sufficient for the committees to converge to the sophisticated voting outcomes. In all eight sessions, not one single subject (i.e., zero out of twenty-four) voted sophisticatedly on the first meeting (play of the game). Across the five sessions using the “fixed” preference assignments there are ten subsequences where the preferences are the same in at least two consecutive rounds. In all ten cases, the committees converge to the sophisticated outcome regardless of whether the preference profiles are public or private information. Second, the fixed repetition protocol is not a necessary condition for sophisticated outcomes to obtain, but it is considerably more difficult with random repetition, and such outcomes are only observed in the public information treatments. In particular, the proportion of voters who vote sophisticatedly is significantly less with random repetition compared to fixed repetition.43 Third, there are significant differences across individuals. Some subjects learn to vote sophisticatedly and some do not. While sophisticated voting becomes widespread with fixed repetition, it is by no means universal. Principal Findings 1. If voters have little or no information about other voter’s preferences, they do not behave according to the backward induction logic of sophisticated voting. Instead, their behavior is best described by a combination of simple rules of thumb for decision making under complete ignorance. 2. If voters have an opportunity to learn about the preferences of other voters, behavior is largely consistent with sophisticated voting, at least in relatively simple agendas. 2.2.3 DYNAMIC BARGAINING IN THE SHADOW OF A VOTING RULE The Baron-Ferejohn (BF) Bargaining Model The Baron-Ferejohn (1989) bargaining model is a blend between the Rubinstein-Stahl bargaining game and the RomerRosenthal monopoly agenda-setter model. The Romer-Rosenthal setter model is the political science version of the ultimatum game but in a political model with single peaked preferences and a voting rule. The Rubinstein-Stahl bargaining model is the infinite-horizon limit of alternating offer games, of which the ultimatum game is the

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shortest possible. In Romer-Rosenthal, the game ends with a status quo outcome if the setter’s proposal is voted down.44 But in models of the BF tradition, the process of offer and accept/reject may continue indefinitely, with the proposer typically changing over time in the event the proposal is rejected. In this repeated version of bargaining, a much richer set of strategic possibilities emerge. In the setter model, there are four critical factors that determine the equilibrium: the set of feasible alternatives, the policy preferences of the setter, the voting rule, and the policy preferences of the voter who is pivotal under that voting rule. In moving from the one-shot setting to a repeated version of committee bargaining, some additional structure is required to capture several new factors that come into play. These additional factors include the time preferences of the voters, the recognition rule that determines the proposer at each stage as a function of the history of play, and the amendment procedure. The “standard” BF model is limited to purely redistributive policy spaces. In the simplest version of the model, a committee of size n (odd) must decide how to divide a dollar among its members. One of the members is selected at random (recognized) to propose a division, d1 = (d11 , . . . , d1n ). An up-down vote is taken on the proposal. If a majority votes in favor of d1 , it is implemented, the bargaining game ends, and payoffs accrue (players are assumed to have linear von Neumann–Morgenstern utility functions over their share of the dollar). On the other hand, if the proposal does not win a majority of votes, the process repeats itself: one of the members is selected at random (possibly the same one) to propose a division d2 = (d21 , . . . , d2n ). Another up-down vote is taken, and if a majority votes for d2 , the game ends and payoffs accrue, with utilities for member i being discounted by a factor δi ∈ [0, 1]. This process repeats itself until some proposal eventually wins a majority. Payoffs are 0 if no proposal ever wins. One can obtain many variations of this basic game by changing the recognition rule (time dependence, unequal recognition probabilities), the time preferences of the players, the voting rule (weighted voting, super-majority rule, veto players, etc.), allowing for amendments before the vote, having a terminal period T , specifying a status quo in the event no proposal wins, concave utilities, more general feasible sets, and so forth. While BF games have many similarities to discounted Rubinstein bargaining, they are different in several important ways. First, there are typically an infinite number of subgame perfect equilibria. These arise for the following reason. Equilibrium proposals will offer positive shares of the pie to just enough members to obtain a bare winning majority because buying off additional members is costly but does not change the probability the proposal wins. Therefore, the choice of which members the proposer excludes can, in equilibrium, favor some members over others. In turn, this favoritism (or retaliation) can depend on the history of prior proposals and votes. This allows a huge degree of freedom in the construction of equilibria that was not available in the simple two-person alternating-offer game. This suggests that laboratory testing of the theory may be especially important in establishing an empirical basis for ruling out at least some of these alternative equilibria. Theoretical selections have been proposed. Baron and Kalai (1993), in particular, prove that the simplest equilibrium corresponds to the one that is the natural extension of the unique subgame perfect equilibrium in Rubinstein’s game. It is very easy to describe for the standard BF model if recognition probabilities are uniform and all voters are risk neutral and have the same discount factor and the voting rule is majority rule. In that case, the equilibrium reduces to one in which the proposer offers just a large enough share of the pie to a randomly selected coalition of (n − 1)/2 other members so that each of the members of the coalition is

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exactly indifferent between voting for or against the proposal. The remaining share of the pie is kept by the proposer. All members out of the coalition vote against the proposal and all members in the coalition vote for the proposal. If a proposal fails, then the next randomly selected proposer makes a similar proposal, and so on. By the symmetry of the game and since there is no delay in this equilibrium, the value of the game to each member of the committee is just 1/n. Hence, the proposer must offer δ/n to each member of his coalition in equilibrium, and keeps a share equal to 1 − [(n − 1)/2](δ/n).45 A second difference—one that can be convenient for laboratory testing—is that the stationary equilibrium solution is typically well defined even in the limit where the future is not discounted at all (δ = 1). For example, if n = 3 and δ = 1 the proposer offers one of the other members a share of 13 and keeps a share equal to 23 . BF Experiments There have been several laboratory studies of the Baron-Ferejohn bargaining model and variations of it. In all versions of these studies, the equilibrium of the standard BF game has had four main properties. First, there is a proposer advantage, in the sense that a player is better off being the proposer than not being the proposer. Second, there is no delay in the equilibrium, so proposals should always pass. Third, there is full rent extraction, in the sense that the members of the proposer’s coalition are exactly indifferent between voting for or voting against the equilibrium proposal. Fourth, only minimum winning coalitions arise. That is, the proposer offers shares only to enough other members to get a bare majority (or, in the case of a super majority, only the minimum number of votes to pass). These four properties are also properties of most of the alternating-offer bargaining games that have been studied in the laboratory, and the first and third properties are also properties of the Romer-Rosenthal setter model that was studied in the Eavey-Miller experiment. Thus it should come as no surprise that many of the findings of those experiments find parallels to results from BF experiments. Three parallels are particularly important. First, there is a proposer advantage, but it is less than what the theory predicts. Second, there is sometimes delay. Third, there is not full rent extraction. Clearly, models that predict full rent extraction by proposers fare poorly if responders are allowed to veto the outcome, either individually or as part of a blocking coalition. Just like in the ultimatum game or more complicated alternating-offer games, this means the proposer in all these settings must trade off the value of a better proposal against the risk of having it voted down. There is indeed strategic risk in these environments. Whether it is due to social preferences or some other source is still an open question and has been an area of intense study in behavioral economics. For whatever reason, such risk exists, and it implies unpredictability about what responders will or will not vote for. Given that different proposers will tolerate different amounts of risk and presumably have different priors about the responders’ range of acceptable offers, this will necessarily lead to some delay. However, while this implies failure of the second and third theoretical properties of equilibrium, the first observation should still be true: a proposer advantage should still be observed. And indeed that is the case, although it is diminished somewhat because of the blocking threat. The First Laboratory Study of BF The pioneering laboratory study of BF models was McKelvey (1991), which provides a simple test of whether the stationary equilibrium is a good predictor of behavior and outcomes. That paper does not investigate a divide-the-dollar environment but instead investigates what is essentially the simplest possible BF environment: three alternatives {A, B, C} and three voters {1, 2, 3}.

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Voter preferences over the three alternatives lead to a Condorcet cycle. The von Neumann–Morgenstern utilties for voter 1 are (1, 0, v3 ) for alternatives A, B, and C, respectively; the corresponding payoffs for voters 2 and 3 are (v1 , 1, 0) and (0, v2 , 1), where vi ∈ (0, 1) for i = 1, 2, 3. The unique stationary subgame perfect equilibrium has proposers always proposing their most preferred outcome (1 proposes A, 2 proposes B, and 3 proposes C). However, in contrast to the “no delay” property in subsequent BF experiments, there is mixing at the voting stage and thus there can be delay in equilibrium. The stationary equilibrium makes sharp predictions about the distribution of proposals, final outcomes, expected delay, and so forth, which are tested using data from his experiment. The design of the experiment varies (v1 , v2 , v3 ) and also looks at a four-alternative game where three of the alternatives cycle, exactly as in the first part of the design, and the fourth alternative is “fair” in the sense that it gives everyone the same payoff. In all treatments the discount factor is 0.95 and subjects are paid in lottery tickets to induce risk neutrality. There are four main findings. The sharpest of these findings is in the four-alternative committees, where unfair outcomes are predicted to arise 100% of the time. Indeed, unfair outcomes are observed over 95% of the time, lending strong support for the stationary equilibrium. In contrast, with the three-alternative committees, there are three features of the data that clearly contradict the predictions of the stationary equilibrium. First, committee members almost never propose the alternative corresponding to min{v1 , v2 , v3 } if that minimum is very low (which it is for most of the three-alternative committees). In other words, one of the subjects consistently proposes his or her second-ranked alternative, thereby avoiding the lowball “offer” to a coalition partner that would result from proposing his or her top-ranked alternative.46 Because such a proposer’s second-ranked alternative corresponds to one of the other members’ top-ranked alternatives, this virtually guarantees the proposal will pass, so this is the “safe” strategy for such a proposer. Second, proposals are accepted with higher probability than theory predicts (partly because safe strategies are used). Third, there is significantly less delay than predicted by the theory. McKelvey suggests that these three departures from the stationary equilibrium could be due to risk aversion—that is, a failure of the lottery procedure to induce risk neutral preferences, a failure that has been documented elsewhere.47 The findings are also consistent with subjects maximizing an objective function that includes a preference for bilateral fairness (outcomes that are fair to one’s coalition partner) or a preference for efficient outcomes (i.e., outcomes that maximize the total payoff to the group). Divide-the-Dollar BF Experiments In the remaining versions of BF games that have been conducted in the laboratory, the theoretical equilibrium has the four properties of proposer advantage, no delay, full rent extraction, and minimum winning coalitions. The first48 of these experiments (Fréchette, Kagel, and Lehrer 2003) compares open versus closed rules in the proposal/amendment process. The closed rule was described earlier as the standard BF model. The open rule differs by giving a second randomly selected proposer the option of either seconding the proposal (i.e., forcing a vote on the first proposal) or offering a substitute proposal. In case of a substitution, there is a vote between the original proposal and the substitute. The winner becomes the standing proposal, the discount factor is applied to payoffs, and another randomly selected proposal is chosen to either move the question or offer a substitute. The procedure continues until there are no further substitutions and a proposal is passed. There are

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two differences in the equilibrium of the two games. First, the open rule dilutes proposer power. For, example, in their five-member closed-rule committees with δ = 0.8, the proposer’s equilibrium share is 0.68, and his two coalition partners each receive 0.16; but with open rule the shares are 0.52 and 0.24, respectively. The second difference is that the open-rule equilibrium can lead to delay. This occurs if a noncoalition partner (i.e., someone whose proposed allocation equals zero) is selected as the second proposer, which happens with probability 12 . In that case, a substitute amendment will be offered, forcing delay. A number of findings are reported. As in the earlier McKelvey study, they observe— in both open- and closed-rule committees—a proposer advantage, but less than would be predicted by theory; that is, full rent extraction does not occur. Second, the proposer advantage is greater under a closed rule, and this gap widens with experience. Third, the closed rule produces no delay, and the open rule produces considerable delay. Regarding the latter, they find less delay than predicted (as in the McKelvey study). Fourth, proposals converge with experience to ones with minimum winning coalitions.49 Fréchette (2009) looks more deeply into the dynamics of behavior across the fifteen rounds. He observes that initially proposers demanded approximately the same shares in both the open and closed rules, and it is only after time that the gap appears, as closed-rule proposers increased their demands and open-rule proposers decreased their demands. Second, while minimum winning coalitions are predominant by the later rounds, they are less common in the early rounds. He shows that a beliefbased learning model based on Cheung and Friedman (1997) can account for these trends. Fréchette, Kagel, and Morelli (2005a, 2005b) report results from an experiment designed to test the separate effects of bargaining power and recognition power in a legislature with different-sized parties who have strong party discipline (i.e., always vote as a block). Bargaining power is measured directly in terms of the size of the voting block. Recognition power is measured by the probability of being the proposer in any stage of the BF game. The analysis focuses on three parameter configurations. The first (baseline) is the standard BF model with three member committees. In this case all voters have equal voting weights and equal recognition probabilities. The second 5 , and one small treatment has two large parties, each with a voting block weight of 11 1 party with a voting block weight of 11 , and all parties have recognition probabilities equal to 13 . The equilibrium strategies are identical to the first treatment: all proposers receive a share of 0.67, regardless of whether they are one of the large parties or the small party, and they choose their coalition partner randomly. The third treatment is the same as the second treatment, except the recognition probabilities are proportional to the voting-block size. Again, the equilibrium solution is the same. While these three treatments produce no effects under the BF model, they do produce large effects under a competing model of coalition formation that has had a significant impact in political science: Gamson’s law. Gamson’s law predicts that political spoils will be divided in a coalition in proportion to the voting blocks of its constituent members and that the proposer will always choose the “cheapest” coalition partners (the latter also being true for BF). Thus, in treatments 2 and 3 with unequal voting weights, Gamson’s law predicts that only coalitions consisting of one large and one small party will ever form, and the spoils will always be divided such that 56 goes to the large party coalition member— regardless of who the proposer is.50 While the results do not conform exactly to the BF equilibrium predictions (for largely the same reasons as in Fréchette, Kagel, and Lehrer 2003), the findings are nowhere close to the predictions of Gamson’s law, except for

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the baseline treatment. However, there is significant proposer power with experienced subjects even in the baseline session, contradicting Gamson’s law. One final treatment was conducted with equal voting weights but a discount factor δ = 0.5. This change in the discount factor predicts no change in outcomes under Gamson’s law but predicts greater proposer power under the BF hypothesis. They find that with the lower discount factor, coalition partners are willing to accept lessgenerous proposals resulting in an increase in proposer power, at least for experienced subjects. However, the effect is considerably smaller than the predicted equilibrium change. The class of bargaining protocols laid out in BF is obviously only one of many possibilities. In “real” political bargaining, the structure is not always that clear, and we know from theoretical work on noncooperative bargaining in economics that the exact details of the bargaining protocol can greatly affect outcomes. To the extent that we hope these models (and experiments) can tell us something useful about legislative politics, there is an argument for (1) considering other plausible models of the political bargaining process and (2) trying to compare findings from experiments to field observations of political bargaining outcomes in governments. Morelli (1999) proposes an alternative bargaining format, demand bargaining (DB), whereby voters are randomly ordered, and then make sequential demands following that order until there is a collection of feasible demands (i.e., sum to less than or equal to 1) from a coalition that holds a majority share of the votes. If, after everyone has made their respective demands, there is no feasible winning coalition, then the process starts all over again with discounted payoffs. The equilibrium allocations are indeed affected by the bargaining rules, with BF alternating offer rules generating greater proposer power, and the demand bargaining rules producing equilibrium allocations that are proportional to voting weights, with no first-mover advantage. Fréchette, Kagel, and Morelli (2005c) design an experiment to compare outcomes under the two protocols.51 They run sessions with five-member committees and no discounting and with two different sets of parameters, one where all voters have equal weights and another where there is one powerful “apex” voter (with three times the voting weight of the smaller, “base” voters). Several sessions used experienced subjects and all sessions consisted of ten elections, using a random matching protocol. Subject payments were based on one randomly selected election. One difference they observe that is not predicted by the theory is a significant difference in the frequency of delay between BF and DB. There is almost never delay with DB (less than 5% of the elections), but delay is frequent with BF (about 40%), with essentially no experience effects.52 Some of the BF elections with experienced subjects required as many as seven rounds to reach agreement.53 Minimum winning coalitions are generally observed in both treatments, with increasing frequency with experience. Concerning allocations, consistent with past findings, most proposers in the BF committees have some proposal power (receive higher shares than their voting share in a coalition), with the exception being the apex proposers, who receive less than their voting share as proposer. Also consistent with past findings, all the BF proposers have less proposal power than predicted by the stationary subgame perfect equilibrium; correspondingly, coalition partners in the BF committees receive more than their equilibrium allocations. In contrast, proposers in the DB committees earn more than their equilibrium shares (significantly more when experienced). That is, the first movers have proposer

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power, while the theory predicts they should receive allocations equal to their voting weights.54 This leads to a central conclusion of the experiment: There is significantly less difference in outcomes between the two bargaining protocols than is predicted by theory. The authors then consider the implication of this main finding for the interpretation of regression results from field data. Conducting regressions with their laboratory data, similar to those used with field data to compare DB and BF protocols (Ansolobehere et al. 2005; Warwick and Druckman 2001), they find that such regressions fail to distinguish between the models. On one hand, this casts doubt on the empirical exercise of trying to find out which model corresponds most closely to political bargaining phenomena; on the other hand, the overall finding suggests that perhaps some better intermediate model is lurking in the shadows waiting to be discovered. Finite Horizon Experiments Diermeier and Morton (2005)55 and Diermeier and Gailmard (2006) also report a lack of proposer power in their studies of legislative bargaining with asymmetric voting weights and recognition probabilities. Both studies employ a much different experimental protocol. The former looks at finite-horizon bargaining games (maximum of five-rounds); the latter allows only one round and varies the continuation payoffs to committee members in the event the proposal fails. Because they are only one round, the Diermeier and Gailmard study is more closely related to the ultimatum game literature.56 The former paper examines how proposal and voting behavior changes when the outside option (status quo) payoff to the proposer is varied and find strong effects that don’t seem to be consistent with social preference models. The latter paper changes all three status quo payoffs simultaneously and investigates how behavior changes as the sum of the payoffs in the status quo changes. They find that the standard equilibrium model works better when the status quo payoffs are relatively high. Legislative Bargaining with Public Goods Fréchette, Kagel, and Morelli (2012) investigate the effect of adding a public good dimension to the static BF divide-thedollar game, following very closely the model of Volden and Wiseman (2007, 2008). In their experiment, a five-member legislature is faced with an exogenous budget which is to be allocated between investment in the public good and private good transfers to the members of the legislature. Production technology is linear: each unit invested in the public good yields 0.7 units of the public good. Preferences are linear in the public and private goods and identical across agents. The marginal rate of substitution between private and public good is α/(1 − α), so higher values of α indicate a lower preference for public good production. The BF bargaining model using a closed rule, majority voting, and the uniformly random recognition rule is followed, and the discount factor is δ = 0.8. Because of the linearity of the environment, the predictions of the model are straightforward. For low values of α, the equilibrium proposal is to invest everything, with no private transfers. For sufficiently high values of α, the equilibrium proposal is to invest nothing, with minimum winning coalition transfers equal to the standard BF solution in the divide-the-dollar game. For intermediate values of α, the equilibrium allocation involves both positive amount of public good and positive transfers to a minimum winning coalition. In this intermediate range, the investment in public good increases in α, which is somewhat counterintuitive. For similar reasons, the equilibrium private good allocation to the proposer is nonmonotonic. Figure 6.5 illustrates the nonmonotonic relationship between α and the equilibrium investment in public good.

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y 1

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Their design was organized in a way to provide a simple test of this nonmonotonic relationship between α and both the level of public good investment and the private good allocation to the proposer. The main finding is that the nonmonotonic relationship is not observed. Contrary to the equilibrium, the observed public good levels are monotone decreasing in α, and the proposer shares are monotone decreasing in α. The proposer shares are also much less than predicted by theory, and the public good levels are generally higher than the equilibrium prediction. In fact, the lowest three treatments are nearly indistinguishable from each other with nearly all the allocation in the public good and proposer private allocations less than 10%. The authors find some evidence of learning in the direction of the theory for the α = 0.55 and α = 0.65 but no such evidence in the α = 0.45 treatment.57 It is likely that there is no learning in the α = 0.45 treatment because full investment in the public good is almost an equilibrium. The proposer has little to lose by proposing full investment; in fact, investing everything is the stationary equilibrium for α ≤ 0.42. This suggests that a quantal response equilibrium analysis of the model might account for this departure from the theory.58 Another possible factor, perhaps related, is that the equilibrium is “weak” in the middle region in the sense that voters are indifferent between voting for and against the equilibrium proposal. We know from ultimatum games and previous BF experiments that such indifference is a problem in the theory: an offer must leave something on the table or there is a high probability it will be rejected, which is also consistent with quantal response models. In the middle region, as long as α is relatively small, say, 0.45 or 0.55, the obvious (and cheap) way to leave money on the table is to invest more than the equilibrium amount in the public good, which is consistent with the data. In the middle region, if α is relatively large, say, 0.65, the obvious (and cheap) way to leave money on the table is to give away a larger share of the private good, which is also consistent with the data. Other findings from the experiment mirror results from divide-the-dollar BF experiments. Delay is infrequent; proposers have some power but less than equilibrium; and minimal winning coalitions are commonly observed. The concept of minimum winning coalition here is a bit different from divide-the-dollar games. For low values of α there are no private allocations. In the middle range of α where the equilibrium public good allocation is strictly between 0 and 1, only the proposer should receive a positive private allocation. For high values of α the minimum winning coalition is the usual simple majority.59

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Principal Findings from BF Experiments 1. There is significant proposer power, which is diminished by having more competitive agenda protocols, such as allowing amendments or following a demand bargaining game form. 2. While proposal power is significant, it is less than predicted by theory. As in ultimatum games, proposers leave some money on the table in order for their proposals to be accepted. 3. There is some delay, but this becomes infrequent with experience, suggesting convergence to the no delay solution. The amount of delay is affected by the agenda protocol. 4. Minimum winning coalitions are most frequently observed, and increasing with experience. Legislative Bargaining in Dynamic Environments All the legislative bargaining experiments described previously involve purely static allocation problems. While the bargaining protocols are multistage games, there is a simple once-and-for-all allocation that is decided by the committee. As noted before, this approach mirrors traditional models of bargaining in economics in static environments, such as the ultimatum game and offer-counteroffer bargaining games. The theoretical literature in political science has recently applied some of the ideas and insights of the static BF model to truly dynamic environments, where the outcome of the bargaining game at one point in time affects the structure of the bargaining problem in later points in time. Dynamic Divide-the-Dollar Games with Endogenous Status Quos The simplest way to introduce dynamics is the case where the committee bargaining takes place in the shadow of a status quo and the status quo is determined endogenously by outcomes of the bargaining game in earlier periods. Battaglini and Palfrey (2012) report the results of an experiment with exactly this kind of environment, following a game similar to the dynamic divide-the-dollar game first studied by Kalandrakis (2004). In that model, a legislature or committee of n members must decide in each of an infinite number of periods how to divide a fixed pie into n parts, operating under majority rule. If we denote the allocation in period t by xt and the proposed allocation in period t + 1 by yt+1 , then the outcome in period t + 1 is given by xt+1 = yt+1 = xt

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of the outcomes quickly converges to a rotating dictatorship: whoever is the current proposer in period t proposes to have a share of 1 and to everyone else, 0, and the proposal always passes. Battaglini and Palfrey (2012) study several variations of this game in the laboratory, inducing the discounted infinite horizon with a constant random stopping rule, δ. In the equilibrium they analyze, voters mix 50–50 if they are indifferent between the proposal and the status quo, and proposers who are indifferent between offering two proposals propose them with equal probabilities. The first two variations limit the set of possible allocations to only four, which simplifies the theoretical analysis and also simplifies the decision problem for the subjects. The four possible allocations in variation 1 are a= b= c= d=

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  c = 0, 12 , 12   d = 12 , 0, 12 The only change here is that the unequal allocations are now split between two members of a minimal winning coalition. This seemingly minor change in payoffs has a huge effect on the equilibrium. In this case, there is no longer a Condorcet winner. Indeed, now a is a Condorcet loser. As a result, it can be shown that the equilibrium involves randomly alternating between allocations b, c, d. Two sessions were conducted for each of variations 1 and 2. In each session subjects played one of the variations ten times with random rematching and a discount factor of δ = 0.75. The variation 2 findings were largely consistent with the theory. Looking at the empirical transition frequencies, if the current status quo was a majoritarian allocation (b, c,or d), then the outcome in that round was nearly always (98% of the time) majoritarian. In contrast, the egalitarian status quo was unstable, with outcomes moving from a to a minimum winning coalition half the time. In fact, 70% of the proposals were for minimum winning coalitions when the status quo was a.

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The results for variation 1, where a is a Condorcet winner, were somewhat further from the equilibrium. On one hand, a was a very stable outcome, as predicted. When a was the status quo in period t, the outcome was nearly always a (94% of the time). However, the nonegalitarian outcomes were less stable. When the status quo was b, c, or d, the outcome was an unequal allocation 62% of the time. Thus, what is observed in the long run when there was a Condorcet winner is that if the status quo is an unequal allocation, then with fairly high probability it will bounce to a, in contrast to the theoretical prediction that there are two absorbing sets of allocations, {a} and {b, c, d}. Nearly any model introduces some error, or “noise,” into the proposal, and voting strategies in the game would predict transitions of this kind. With this in mind, the authors define a generalization of quantal response equilibrium that applies to Markov equilibria in infinite horizon games such as the ones studied in the paper. This equilibrium, called Markov Logit equilibrium (MLE) applies the framework of the agent quantal response equilibrium (McKelvey and Palfrey 1998), so it combines sequential (quantal) rationality and stationarity of strategies and the Logit specification of stochastic choice. They solve numerically for the MLE value function, and players Logit-best-respond given the MLE value function. For any value of the Logit noise parameter, λ, the model predicts a stochastic long-run alternation between the absorbing regions in variation 1, qualitatively similar to the one observed in the data; and it predicts relative stability of the {b, c, d} region in variation 2. They estimate the value of λ that best fits the data and report a close match between MLE and data. The third variation was much closer to the Kalandrakis model of divide-the-dollar because proposals were not constrained to be one of four proposals but could be essentially any three-way split of the dollar, using a relatively fine discrete grid.60 The equilibrium of this game is similar, but not identical, to Kalandrakis, partly because of the discrete grid on allocations. Recall that in the Kalandrakis equilibrium, the prediction is to rotate between the vertices of the simplex, corresponding to one member receiving the entire dollar. In the equilibrium for the discretized version of the game, the equilibrium involves rotations between regions close to the vertices, but not exactly at the vertices. Three sessions were conducted for this divisible variation, two with δ = 0.75 and one with δ = 0.83. In both cases, there was a lot of clustering and stability to allocations far away from the vertices, in contrast to the theory. In fact, outcomes close to the vertices were quite rare (less than 20% of the time). Outcomes were either perfectly or nearly egalitarian more often than that, and over 60% of the allocations were approximately minimum winning coalition allocations, where two of the members received large allocations and the third member received a zero or token allocation. Using numerical computations to characterize neutral solutions when utilities are concave rather than linear, the authors are able to show that as concavity increases the long run distribution of allocations becomes more equitable. Figure 6.6 shows the expected long run distribution of allocations when voters have CRRA utility functions with parameter γ , where linear utility corresponds to γ = 0. In this sense the data suggest that perhaps the linear utility assumption is too strong. Using MLE as an error structure the authors estimate the degree of concavity, assuming constant relative risk aversion. Their risk-aversion estimate (approximately a square root utility function) is close to what has been found across a broad range of other experimental studies. Concavity is also consistent with the finding in variation 1, that the egalitarian regime is much more stable than the regime corresponding to rotation

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between unequal allocations. One final note about the behavior in these experiments is that behavior is largely consistent with a model of perfectly selfish players, with little indication of other-regarding preferences. Voting behavior, in particular, can be explained quite well by a model of pure self interest.

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Principal Findings for Dynamic Divide-the-dollar Games 1. Allocations over time are “smoother” than predicted by the theory. This is consistent with voters having concave utility functions. 2. Minimum winning coalitions are observed about as much as in BF bargaining games. 3. Proposals are usually accepted. Egalitarian proposals are fairly common and are virtually always accepted. Dynamic Legislative Bargaining with Durable Public Goods Battaglini, Nunnari, and Palfrey (2012) propose a framework for studying the political economy of durable public good production along the lines of models of economic growth. They establish some basic theoretical results about the effect of the voting rule on the investment path of the public good when the path is chosen over a sequence of periods with a legislative bargaining game. Specifically, the environment consists of many citizens divided into n equally sized districts, each with a single representative in the legislature. All citizens have the same per-period utility function, which is linear in the private good with an additively separable concave utility, u(yt ), for the current stock, yt of the durable public good. There is an infinite horizon and a discount factor δ. In each period, there is an endowment equal to W and a policy in period t is an n + 1 vector, where the first component equals the investment in the durable public good, It , and the last n components, xt = (x1t , . . . , xnt ), are the private good transfers to each district. The investment increases the stock of the durable public good, and the durable public good depreciates at rate d in each period. Hence, the stock of public good in period t is equal , and an allocation sequence is {xt , yt }∞ to yt = (1 − d)yt−1 + It  t=1 . Feasibility requires allocation sequence as xt ≥ 0, yt ≥ 0, and yt + in=1 xi t = W, for all t. Voter i values an t−1 the discounted sum of per-period utility of the sequence, that is, ∞ [xi t + u(yt )]. t=1 δ The bargaining game is simple. In each period one of the n legislators is randomly selected to make a proposed allocation (yt , xt ), and an up-down vote is conducted in the legislature under a closed rule. Voting follows a q-r ule, where the proposal passes if and only if it receives at least q votes in favor. If it fails, then a status quo outcome occurs. They consider a simple exogenous status quo outcome, (y0 , x0 ), where y0 = 0 and xi t = W/n for all i . There are several theoretical properties of the model that can be examined by a laboratory experiment. First, for all values of q and other parameters in the model, the symmetric continuous Markov perfect equilibrium investment paths are inefficient. Second, this inefficiency decreases with q.61 In the case of unanimity rule, the steadystate level of the stock of public good is actually equal to the optimal level, although the speed of approach to the steady state is too slow, as proposers skim off some resources for private consumption in each period. The article reports results from an experiment with legislatures of size n = 5 and three different voting rules: simple majority rule (q = 3), unanimity rule (q = 5), and dictatorship (q = 1). In all the treatments, there is zero depreciation (d = 0), square root utility functions, and a discount factor of 0.75 is implemented using a random stopping rule with constant probability of 14 . Figure 6.7 shows the median time paths of yt for the first ten periods for each of the three q rules. The theoretical equilibrium levels of yt are marked in the figure. There are several main findings. First, consistent with the Markov perfect equilibrium, the level of investment is far below the efficient level and converges over time

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70 U Obs Mdn U theory M Obs Mdn M theory D Obs Mdn D theory

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Figure 6.7: Theoretical and median time paths of yt for different voting rules. Source: Battaglini et al. (2012).

to levels much closer to the steady state of the Markov perfect equilibrium.62 Second, the unanimity voting rule produces the most efficient outcomes, dictatorship, the least efficient, and majority rule, in between, as predicted. Investment with q = 3 (majority) levels off at nearly triple the size compared to q = 1 (dictatorship). Investment with q = 5 (unanimity) converges to approximately six times the size compared to q = 1. Third, the path of convergence to a steady state is different from the theory. There is overshooting—that is, the legislatures overinvest in early rounds and then disinvest in later rounds. In all three q treatments, the trajectory has the same pattern of early overinvestment followed by later disinvestment. Fourth, most proposals pass, as is consistent with the findings in the static games discussed earlier. Fifth, approximately minimum winning coalitions are the norm. While the proposals observed often have positive transfers to all districts, most of the transfers are concentrated in a minimum winning coalition. Battaglini, Nunnari, and Palfrey (2014, 2015) consider a variation of the model in which the investment in the stock of public good in each period is made in a completely decentralized way, with each district deciding independently how much of their (equal) share of the endowment (W/n) to invest in the public good. This produces an economic environment that is a dynamic voluntary contribution game, where the public good is durable, rather than the standard static model, where the public good is nondurable. The voluntary-contributions mechanism is similar to many of the more traditional static public goods games, as surveyed in Ledyard (1995). The main difference is that with a durable public good, the public good level increases over time, and current contributions add to the stock of the public good, which produces a stream of public benefits over time. In the traditional static public goods experiments, public good contributions produce benefits only in the current period. Often those traditional public goods experiments are

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repeated several times in order to study learning dynamics, but there is no accumulation of stock; the level of public good is zeroed out at the start of each period. The durable public goods experiment with decentralized public good investments is reported in Battaglini, Nunnari, and Palfrey (2015), and the design is organized in a way to examine the theoretical results reported in Battaglini, Nunnari, and Palfrey (2014). The latter paper characterizes the symmetric continuous Markov perfect equilibria of the game and obtains comparative static results with respect to the discount factor, the rate of depreciation, the group size, and the concavity of the utility function. It also considers two different technologies of public good production, depending on whether investments in the public good are reversible. In particular, they show that the reversible case leads to lower public good contribution than the irreversible case. This comparison is especially stark in the case of no depreciation, so the experiments focus on that case. The experiment reported in Battaglini, Nunnari, and Palfrey (2015) varies the group size between three and five and includes both reversible and irreversible investment treatments. The discount factor of δ = 0.75 is used in all treatments. The basic procedures are similar to the legislative bargaining, with the only difference being the voluntary contribution mechanism instead of the legislative bargaining mechanism. The two main findings are that (1) there are significantly more contributions with irreversible investments than in the reversible case, and (2) there are also more contributions with n = 5 than with n = 3, but the difference is small and not significant. Figure 6.8 shows the median time paths of yt for the first ten periods. The theoretical equilibrium levels of yt are marked in the figures. The experiment generally finds support for the predictions of the Markov perfect equilibrium but with similar caveats as described earlier with respect to the experiment of Battaglini, Nunnari, and Palfrey (2012). Principal Findings for Durable Public Goods Experiments 1. Most proposals are for (approximately) minimum winning coalitions and most proposals pass. 2. The proposer has significant proposer power. 3. Efficiency is increasing in the q rule, as predicted by the Markov perfect equilibrium, and is much less than the optimal solution. 4. The public good level converges to approximately the long-run steady state of the Markov perfect equilibrium.

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5. The dynamics of convergence is characterized by overshooting the steady state in early periods and then either leveling out (if investments are irreversible) or drifting back down through disinvestment toward the equilibrium steady state. 6. Voting behavior is generally consistent with long-run optimal behavior, in the sense of the Markov perfect equilibrium value function. 7. Contributions are higher when investments in the public good are irreversible.

3 ELECTIONS AND CANDIDATE COMPETITION While the first wave of experiments in positive political economy centered around cooperative game theory and unstructured bargaining in committees under majority rule, a second wave of political science experiments followed quickly on the heels of the first, and investigated the question of Condorcet winners and the majority rule core in the context of competitive elections rather than small committees. These studies address many of the same questions that have received the attention of empirical political scientists. The key questions we will focus on here are: (1) spatial convergence of candidate platforms in competitive elections; (2) retrospective voting; and (3) the importance of polls in transmitting information to voters and coordinating voting behavior in multi-candidate elections. 3.1 The Spatial Model of Competitive Elections and the Median Voter Theorem 3.1.1 TWO-CANDIDATE ELECTIONS WITH A MAJORITY-RULE CORE The median voter theorem says that under certain conditions, in two-candidate winnertake-all elections, candidate platforms will converge to the ideal point of the median voter. The theorem applies under fairly general conditions in one-dimensional policy spaces with single-peaked preferences and under more stringent conditions in multidimensional policy spaces. Basically, if Condorcet winners exist, they correspond to the symmetric pure-strategy Nash equilibrium of the game between two officemotivated candidates. Casual observation indicates significant divergence of candidate and party platforms, even in winner-take-all elections. Laboratory experiments can help us understand why this may happen by providing some empirical evidence about the conditions required for convergence. There has been extensive work on candidate competition where voters have Euclidean preferences and a Condorcet winner exists. The early contributions to this effort are mostly by McKelvey and Ordeshook, and much of this is detailed in their 1990 survey. The focus of this work has been on questions about the informational conditions that are needed for convergence to equilibrium in candidate competition games. The simplest and least challenging environment is one where the candidates have complete information about voter preferences, so the existence and location of the Condorcet winning platform is common knowledge.63 This is the environment used in their initial study (McKelvey and Ordeshook 1982), which was further simplified by having only candidates as subjects, with the behavior of five voters implemented by automatically voting for the closest candidate. There were ten repetitions of the candidate-competition game. In each play of the game, the candidates simultaneously chose locations in a two-dimensional space and were then told the electoral outcome and the location chosen by the other candidate. A candidate received a positive payoff whenever he or she won an election, with ties broken randomly if both chose the same location.

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Outcomes converged to the Condorcet point.64 The distribution of outcomes in the last five repetitions is shown in Figure 6.9. More than half of the observations are exactly at the majority-rule core point. More challenging environments involve relaxing the assumption that candidates have complete information and implementing voting behavior with human subjects rather than by artificial actors. Principal Finding for Competitive Elections with a Core •

When a majority-rule core point exists, with enough repetition and learning, the outcomes of an election game between two candidates converges to the Condorcet winner. If a majority-rule core point fails to exist, outcomes are concentrated in a central region of the Pareto set, as if generated by the distribution of locations in a mixed-strategy equilibrium.

3.1.2 INFORMATION AGGREGATION BY PREELECTION POLLING The first experiment where polls are used to aggregate information were conducted by Plott in the mid-1970s, with the results later published in Plott (1991). In these experiments, there were between 19 and 41 voters (human subjects) with ideal points in a two-dimensional space, configured so that there was a Condorcet winning point. There were two office-motivated candidates,65 who were uninformed of the voters’ ideal points. All they knew was that the policy space was a specific rectangle in twodimensional space. In each election, candidate positions were initialized near the edge of the policy space, far from the Condorcet winner. At any time, either candidate could revise his or her platform by announcing a new (tentative) location. Candidates could

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also query voters about how many would prefer them to move in some direction. In addition, public straw votes were conducted periodically by the experimenter, based on the current (tentative) platforms of the two candidates. At the end of a prespecified time period, each candidate announced his or her final position, which could not be changed. The election was then held, with the winner receiving $10 and the loser, $1. The data include ten such elections with two candidates. In seven of ten elections, the outcome was exactly the Condorcet point. The other three elections resulted in outcomes very close to the Condorcet point. McKelvey and Ordeshook (1985a, 1985b) push the information question further by studying elections where voters have poor information about the candidate locations. In these studies, they pursue a variety of issues, mostly related to the question of how much information was required of voters and candidates in order for competitive elections to converge to the Condorcet winner. Perhaps the most striking experiment was reported in McKelvey and Ordeshook (1985b) study of candidate competition in a one-dimensional policy space. In this experiment, not only did candidates have no information at all about voters, but only half of the voters in the experiment knew where the candidates were located. The rest of the voters were informed only about the left-right ordering of the candidates. The key information-transmission devices they explored were polls and interest group endorsements. In a theoretical model of information aggregation adapted from the rational expectations theory of markets, they proved that this information alone is sufficient to reveal enough to voters that even the uninformed voters behave optimally, that is, as if they were fully informed.66 A corollary of this is that the candidates would converge to the location of the median voter. Two sessions were conducted, each with two candidates and between forty and fifty voters. The game was repeated eight times to allow for learning and convergence. The experiment finds strong support for candidate convergence as if information were fully revealed to voters, and even more surprisingly, they converge very close to the median voter. Figure 6.10 shows the time path of locations of the candidates for each of the two sessions, with MT denoting the ideal point of the median voter, MI denoting the ideal point of the median informed voter, and MU denoting the ideal point of the median uninformed voter.

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However, in an extension of this experiment to two dimensions, candidate convergence is much slower; only half the candidates converge to the Condorcet winner with replication. A number of studies have followed up on this theme of limited-information elections. Dasgupta and Williams (2002) also explore the information transmission properties of polls when some voters are informed and others are not. Their setup differs in a number of ways. First, candidates differ along a quality, or valence, dimension as well as a policy dimension. The policy positions of the candidates are assigned by the computer and are publicly known. One is assigned the leftmost position on a one-dimensional scale, and the other is assigned the rightmost position. Second, the quality type of each candidate is unknown to voters at the time of election, but a subset of voters receive some information about the quality of one of the candidates, who has an opportunity to take a costly action to increase voter beliefs about his or her quality.67 A sequence of three opinion polls (straw votes) is then conducted, with all voters participating in the poll and with the outcomes publicly observed. Then the actual election occurs and payoffs accrue based on the outcome. In a manner similar to McKelvey and Ordeshook (1985b), they develop a rational expectations equilibrium model adapted to this environment, in which information of the informed voters is transmitted to the other voters as a result of the polls. The findings are broadly supportive of the information-aggregation properties of polls.68 Principal Findings for Information Aggregation by Preelection Polling 1. Poll information and interest-group endorsements successfully aggregate information even when most voters have very little information a priori. 2. This kind of public information is sufficient to lead to convergence of candidates to the majority-rule core point with sufficient repetition. 3. The convergence to the core point is much slower in two-dimensional policy spaces. 4. The information aggregation properties of polls extends to aggregating information about candidate quality. 3.1.3 RETROSPECTIVE VOTING Political scientists have often wondered whether competitive electoral outcomes can arise purely from retrospective voting. The earlier set of experiments with rational expectations and polls was entirely forward-looking and evaluation of candidates was prospective, very much in the Downsian view of electoral competition. But many leading figures in political science have argued that voter evaluations of candidates are backward-looking, and individual voting decisions depend largely on past records of candidates or current economic conditions.69 Collier et al. (1987) and McKelvey and Ordeshook (1990a)70 study two-candidate elections where voters observe only the payoff they receive from the winning candidate—not even the policy adopted by the winning candidate or the proposed policy (or payoff) of the losing candidate. There are no campaigns or polls. Voters either reelect the incumbent or vote him or her out of office, in which case the other candidate becomes the new incumbent. “Voters observe historical information about their payoffs (real income) derived from the policies (spatial positions) of previous incumbents, but they do not observe these policies directly. Further, to model the situation in which voters do not even conceptualize

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elections in terms of issues, the voters in our experiments are uninformed about the specific relationship (payoff function) between an incumbent’s policy and their welfare. Nor do they know that an incumbent’s strategy concerns the selection of positions in some policy space” (McKelvey and Ordeshook 1990a, p. 283). Candidates are somewhat better informed in that they know what the policy space is, and they observe all the platforms that their opponent has adopted in the past when in office as well as the past election results. However, candidates are given no information about the distribution of voter ideal points or how each voter has voted in past elections. The main finding is that on average candidates converge to the median, even in this information-poor environment (McKelvey and Ordeshook 1990b). In the baseline treatment, candidates receive a dollar for each period they are the incumbent. Approximate convergence of candidate platforms is not immediate but generally is achieved by the end of a session, after between 30 and 45 repetitions. Figure 6.11 illustrates platform convergence for one of the baseline experimental sessions that lasted for 45 periods. The median voter’s ideal point is marked by the dashed line, and the points connected by the solid line represent the winning platforms in each period (which voters of course do not see). Platforms converged almost perfectly to the median voter’s ideal point in the session after a brief period of volatility at the beginning when candidates were still learning. There were several variations on this baseline design to explore the robustness of convergence. In the first extension, candidates have policy preferences. Rather than earning a fixed amount when elected, the incumbent receives a payoff that is a linearly increasing function of the location they choose in the [0, 100] interval. Convergence is still achieved, although more slowly. In the next variation, the two candidates have opposing policy preferences. One candidate’s payoff function is linearly increasing on the [0, 100] interval, while the other’s is linearly decreasing. Again, convergence is achieved, but with a clear alternation of policies. The first candidate tends to choose policies above the median and the opposite for the second candidate, with the biases attenuating over time. Finally, they conducted a variation where the location of the median voter was shifted after period 21, without

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informing the candidates of this shift. Although there is a slight lag, candidates converge surprisingly fast to the new median location. One of the collective implications of these results about elections with limited information is that it appears to be irrational for voters to gather costly information if other sources of information such as polls, endorsements, incumbent past performance, and word-of-mouth are virtually free. This point is made explicitly in Collier and others (1989), which explores the question with twenty-four laboratory elections, where voters are given an opportunity to purchase information about a challenger’s policy if elected, in addition to the free retrospective information that all voters receive about the past performance of the incumbent. That paper and Williams (1991b) explore voter behavior and candidate convergence by giving voters the option to gather costly information about candidates. They find that the amount of information purchased by voters is correlated in the expected (negative) way with the stability of candidate strategies, the imprecision of the information, and the probability of casting a pivotal vote. While this research does not resolve long-standing questions about the responsiveness of democratic institutions, it does add to what we understand about responsiveness by demonstrating conditions under which incompletely informed voters can generate the electoral outcomes that they would have if better informed. This research also informs the debate about the use of the referendum and initiative to determine policy. One answer to the question, is direct legislation a useful mechanism for obtaining policy outcomes that correspond to the will of the majority or is it a way for small, wealthy interest groups to subvert the popular will? is that direct legislation can be both. When voters are poorly informed (or the electoral alternatives are reasonably complex) and there are no effective information cues available, small groups who have enough resources to obtain agenda control can use direct legislation to obtain preferred outcomes. When meaningful cues are available (or the effect of electoral alternatives are easy to understand), then direct legislation can be a useful tool for the implementation of majority-preferred policies. These experiments establish two important facts. First, even in laboratory elections where the stakes are low, election outcomes are well approximated by median voter theory. The Condorcet winner (core) is an excellent predictor of competitive election outcomes. Second, this result is robust with respect to the information voters have about candidates and the information candidates have about voters. Precious little information is needed—a result that mirrors laboratory demonstrations that markets converge quickly to competitive equilibrium prices and quantities, even with poor information and few traders. In the discipline of political science, there has been great concern about how uninformed most of the electorate is about candidates and policy issues. One reason for this concern was a widely shared belief that these information failures could doom competitive democratic processes. The McKelvey and Ordeshook series of experiments casts doubt on this doomsday view. Just as financial markets can operate efficiently with relatively few uninformed traders or with many slightly informed traders, the forces of competition can lead to election outcomes that accurately reflect public opinion, even if voters know very little about the candidates, and vice versa.71 Principal Findings for Information Aggregation by Retrospective Voting 1. Historical information about past performance of candidates is sufficient to lead to convergence of candidates to the majority-rule core point with sufficient repetition in simple environments.

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2. The findings are robust with respect to a variety of modifications of the environment, including unannounced shifts of the median voter location and extreme candidate policy preferences. 3. All the findings of this section are broadly supportive of the hypothesis that competitive elections in sufficiently simple environments can lead to Condorcet outcomes even when voters have very poor information. 3.2 Multicandidate Elections In many elections, more than two candidates are competing for a single position using plurality rule. In these multicandidate elections, there is a natural ambiguity facing voters in the form of a coordination game, and equilibrium places few restrictions on outcomes: that is, there are multiple Nash equilibria. To illustrate this, consider a threecandidate election, with the candidates, A, B, and C having three distinct positions on a one-dimensional issue scale, say, the interval [−1, 1]. Suppose there is a large number of voters with ideal points scattered along the interval. Voters know their own ideal point but have only probabilistic information about the other voters. Then, in a winnertake-all election, for any pair of candidates {i, j }, there is a Bayesian equilibrium in which only these two candidates receive any votes, with each voter voting for whichever of the two is closer to his or her ideal point. This is an equilibrium because it never (instrumentally) pays to vote for a candidate for whom nobody else is voting. Indeed there can be some other equilibria, too (Palfrey 1989; Myerson and Weber 1993), but two-candidate equilibria are the only ones that are stable (Fey 1997). Voters face a coordination problem. Which two candidates are going to be receiving votes? Will a Condorcet winner be chosen if it exists? Forsythe and others (1993, 1996) explore these and other questions in a series of experiments. Their laboratory elections had three categories of voters defined by different preference orders over the three candidates. One group preferred A to B to C. The second group preferred B to A to C, and the third group ranked C first and was indifferent between A and B. The third group was the largest, but was less than half the population. Groups 1 and 2 were the same size. The actual payoff tables and preference configurations are given in Table 6.1. Hence, if voters voted for their first choice, C will win, but C is a Condorcet loser, since it is defeated by both A and B in pairwise votes. There are several equilibria, including the two where type 1 and 2 voters coordinate on either A or B. However, because of the special configuration of preferences and because there is complete information, sincere voting is also an equilibrium, resulting in the Condorcet loser, C, winning.

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The procedures were carefully designed to avoid repeated-game effects, to minimize possible effects of extraneous coordination devices, and at the same time allow subjects to gain experience at the task.72 Each experimental session was conducted with twentyeight subjects divided into fourteen-member voting groups and repeated over a series of twenty-four periods. Thus each session generated data for forty-eight elections, with fourteen voters in each election. Voting groups and preference types were randomly reshuffled after every election.73 First, the authors note that without any coordinating device, there is coordination failure. Some voters in groups one and two vote strategically (i.e., for their second choice, trying to avoid C) but many don’t, and the strategic behavior is poorly coordinated, so as a result the Condorcet loser wins 90% of the elections. Second, they look at three kinds of coordinating devices: polls, past elections, and ballot position. Polls allow the voters in groups 1 and 2 to coordinate their votes behind either candidate A or candidate B. This is indeed what usually happens. The Condorcet loser wins only 33% of the elections. Moreover, when either A or B is first ranked in the poll, the Condorcet loser wins only 16% of the time. Election history also helped with coordination. There was a small bandwagon effect between A and B. Whichever was winning in past elections tended to win in future polls. Ballot position had an effect on voting strategies, but the effect was too small to influence election outcomes. Their second paper looks at alternative voting procedures, comparing plurality rule to the Borda count (BC) and approval voting (AV).74 Both procedures worked better than plurality rule, in the sense that the Condorcet loser was more easily defeated. Both procedures tended to result in relatively close three-way races, with A or B usually winning. Plurality, in contrast, produced close three-way races but with C usually winning. A later study by Bassi (2015) delves more deeply into a comparison of strategic behavior under these three voting rules. That study differs from the earlier studies in three ways: the preference profile, the number of voters (five instead of fourteen), and the number of alternatives (four instead of three). The two profiles employed in the design have the property that iterated deletion of dominated strategies eliminates all but one equilibrium, so the coordination problem created by multiple equilibria is not present. The main finding is that voting is most sophisticated (i.e., most consistent with equilibrium) under plurality and least sophisticated under BC, with AV in between. Rietz, Myerson, and Weber (1998) follow up this experiment with a very similar one that explored whether campaign contributions can have a similar coordination effect. In this variation, before each election, each voter independently decided on campaign contributions. Each voter was allowed to contribute (at real expense) up to $0.20 in penny increments. These contributions could be spread across any subset of candidates or none at all. The total contributions for each candidate were then publicly revealed prior to the election stage. The results were similar to the results from the polling treatment, with the Condorcet loser winning only 33% of the time. The type 1 and 2 voters generally coordinated on whichever candidate, A or B, received the most contributions. Moreover, even accounting for its direct cost, campaign contributions increased coordination enough to lead to higher overall efficiency compared with no contributions. Another question is whether campaign-contribution decisions were consistent with an equilibrium of the two-stage game. The paper does not offer any model of equilibrium for the more complicated game, where the first stage is contribution and the second stage is voting, but instead argues that the contribution levels do not seem irrational, at

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least for the type 1 and 2 voters, in the sense that the marginal benefit from an additional incremental contribution is lower on average than the cost, while the marginal benefit from the last nickel contributed is higher.75 However, this is done as a back-of-theenvelope calculation rather than a careful statistical analysis, and there is a significant free-rider dimension in the contribution stage. There are a number of other papers that conduct experiments on related threecandidate coordination games. The earliest work is by Plott (1991),76 who investigates three-candidate races in a two-dimensional policy space. The setting is different in the sense that candidate locations were endogenous and were sequentially chosen and mixed in with occasional straw votes, with the same procedures as described for the two-candidate elections reported in the same paper. Thus, candidates were adjusting positions over time, and there was a majority-rule core. Unfortunately, there is little guidance in the way of useful predictions based on Nash equilibria. Still, winningcandidate locations tended to converge to the core, but with only slightly more more variance than in the two-candidate baseline treatment. In the ten three-candidate elections, three outcomes were exactly at the Condorcet point and the seven others were close. See Figure 6.12. Rapoport, Felsenthal, and Moaz (1988a, 1991) examine bloc voting in threecandidate elections, where all voters with identical preferences vote identically. Their design considers a variety of preference profiles in order to compare the predictions of several alternative voting models for selecting among the many Nash equilibria of the game. They propose a model of equilibrium selection based on implicit cooperation between voting blocs with similar but not identical preferences. For several of the preference profiles they study, coordination is consistent with their model a large fraction of the time. Gerber, Morton, and Rietz (1998) and Morton and Rietz (2008) explore the multicandidate coordination problem with different electoral institutions. Gerber and others look at cumulative voting when two candidates (rather than one) are to be elected, to see if it can ameliorate problems of minority underrepresentation due to miscoordination.

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Voters are endowed with two votes. In the baseline treatment, they can cast one vote for each of two different candidates, only one vote for one candidate, or no votes for any candidate. In the cumulative voting treatment, they have the additional option of casting two votes for one candidate. The top two vote getters are elected. They use the same preference profile as in Forsythe and others (1993, 1996), and payoffs are additive with respect to the two winners of an election. In the baseline treatment, the theoretical prediction is that C will never win, but C should win under cumulative voting. The data closely match the theory. Morton and Rietz consider runoff elections where winning requires a clear majority. If there is no majority winning in the first round, then the two top candidates engage in a runoff election in the second round. This also helps solve the coordination problem in a similar way to polls: whichever of the two minority candidates is in the runoff wins. To summarize, multicandidate elections are an intriguing and immensely complex brand of coordination problem. Outcomes are extremely sensitive to the fine details of the voting institutions as well as the myriad of coordinating devices related to those institutions (polls, history, party labels, campaign contributions, and even cheap talk). This would seem to be a rich area for both experimental and theoretical research. An obvious direction to explore is to look at the endogenous entry of candidates and endogenous policy positions of candidates. All these experiments fix the number of competing candidates and even fix their policies (except for Plott 1991). Principal Findings for Multicandidate Elections 1. In the absence of coordination devices, simple plurality rule can lead to poor outcomes (Condorcet losers) in multicandidate elections. 2. Very simple coordination devices, such as polls, publicly revealed campaign contributions, and past electoral outcomes, can help alleviate coordination problems. 3. If a Condorcet winner exists, competitive elections under plurality rule with three candidates converge toward the core point but with more variance than in twocandidate elections. 4. Voting rules other than plurality rule (Borda count, approval voting, runoff, etc.) can outperform plurality rule in specific environments. 5. All the preceding results are based on a very limited set of environments that have been studied in the laboratory. 3.3 Candidate Competition with Valence In many elections, candidates are asymmetric. A widely cited source of asymmetry is incumbency. It is generally thought that incumbents have a significant advantage over challengers, above and beyond any advantage (or disadvantage) they may have due to spatial location. Other sources of asymmetries include valence characteristics of candidates, such as a familiar name, movie- or athletic-star status, height, articulateness, and personality traits. The two key aspects of these valence characteristics are (1) most voters value them, independent of the candidate platforms, and (2) they are fixed, rather than being chosen by the candidates. With strategic competition, candidate asymmetries have interesting and systematic implications for equilibrium platforms. These asymmetric contests have been studied recently both theoretically and empirically in game theoretic models by Erikson and Palfrey (2000), Ansolabehere and Snyder (2000), Groseclose (2001), Aragones and Palfrey (2002, 2005), and others.

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Groseclose (2001) and Aragones and Palfrey (2002, 2005) show that valence asymmetries lead to candidate divergence, even in one-dimensional spatial models. The equilibria, which can be either mixed-strategy equilibria or pure-strategy equilibria (if candidates have policy preferences and there is enough exogenous uncertainty), have two interesting features. First, a disadvantaged candidate will tend to locate at more extreme locations in the policy space than the advantaged candidate.77 Second, the extent to which this happens depends, in a systematic way, on the distribution of voters. As the distribution of voter ideal points becomes more polarized (e.g., a bimodal distribution), the disadvantaged candidate moves toward the center, while the advantaged candidate moves in the opposite direction and adopts more extreme positions. Aragones and Palfrey (2004) report the results of an experiment designed to test whether these systematic effects can be measured in a simplified spatial competition environment. Candidates simultaneously choose one of three locations, {L, C, R}. The location of the median voter is unknown, but they both know the distribution. The median is located at C with probability α, and located at either L or R with probability (1 − α)/2. Candidate 1 is the advantaged candidate; he or she wins if the median voter is indifferent (in policy space) between the two candidates, which happens if the candidates locate in the same position or if one chooses L and the other R. Their main treatment variable is the distribution of the median, α, which in different sessions takes on values of either 15 , 13 , or 35 . The equilibrium is characterized by a pair of probabilities of locating at the central location, one for the advantaged candidate ( p) and one for the disadvantaged candidate (q). These equilibrium probabilities are ordered as follows: 0 < q3/5 < q1/3 < q1/5
N B and A voters have more intense induced preferences, so a selfish vote by a B voter is to vote for B and an ethically expressive vote is for A, the group payoff maximizing outcome. They find (1) average turnout about 40%, with somewhat more selfish than ethical voting; (2) insignificant responses of ethical voting to pivot probabilities; (3) large and significant effects of the pivot probability on selfish voting; and (4) the probability of voting selfishly decreases in N A, with no effect of N B . In summary, this study is the cleanest laboratory study yet of expressive voting, but it finds mixed results. The fact that there is nearly as much A voting as B voting suggests there is some degree of ethical voting, but failure of a number of predicted comparative statics cast some doubt on the theory as a useful predictor (or explanation) of how voting outcomes respond to changes in the underlying driving variables such as voting cost, relative party size, and electorate size. Principal Findings for Voter Turnout 1. In experiments with direct costs of voting that are private information (e.g., Levine and Palfrey 2007; Herrera, Morelli, and Palfrey 2014; Duffy and Tavits 2008), many of the comparative statics predictions of the game theoretic instrumental voting model are observed in the data. This includes the size effect, competition effect, and underdog effect. The bottom line is that voters are more likely to vote when they are more likely to be pivotal or believe they are more likely to be pivotal. 2. In most studies there is higher turnout than is predicted in equilibrium with purely instrumental voting.

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3. The Logit quantal response equilibrium model accounts for much of the observed overvoting and also the occasional observations of undervoting. 4. Experimental studies have found important differences in aggregate turnout between proportional representation and winner-take-all elections, and these differences are qualitatively consistent with instrumental voting theory. 5. The low-cost hypothesis about expressive voting over charitable contributions, proposed by Tullock, has relatively little support in the data.

5 INFORMATION AGGREGATION IN COMMITTEES The earlier sections of this chapter discussed experiments designed to address questions of preference aggregation. Given a feasible set of policies, a profile of preferences of the political actors (voters, legislators, etc.), and a political institution, what outcomes will result? Then, as we vary the profile of preferences and the feasible set of policies, fixing the political institution, a picture emerges about how that particular political institution transforms diverse preferences into social choices. This section discusses experiments aimed at understanding an equally important set of questions in social choice theory: how political institutions aggregate the diverse private information of the political actors. While in some cases the aggregation of preferences and information interact in complex ways, most of the political economy research on information aggregation has focused on the pure common values case. The political actors are like minded and thus have identical preferences, and they must decide on a policy where the payoff is uncertain and depends on the state of the world. Although the state is unknown, each actor has some private information about the state of the world. Thus, not only does the committee have limited information about the payoff relevant state, but this information is dispersed across the actors. How do different political institutions pull this information together into a collective decision? Because individuals have identical preferences, one can make unambiguous welfare comparisons across institutions if some institutions lead to more informative decisions than others. That is, in this class of models, an institution is better the more successfully it reflects all of the dispersed information. 5.1 Condorcet Jury Experiments Marquis de Condorcet was the first to formally address this question, and he presented a mathematical argument for the superiority of majority rule as way to aggregate dispersed information when everyone has common preferences. His very simple voting model, the Condorcet jury model (CJM) has survived for more than two centuries and is still the workhorse model of information aggregation in political science. There are two equally likely states of the world, a and b, and each voter (juror) has a privately known clue (or hunch) as to which state of the world is more likely, in the form of a binary signal, α or β. The voters must collectively decide on one of two possible policies, A and B, where all voters prefer A in state a and B in state b. If the individual clues are at all informative (e.g., pr{α|a} = pr{β|b} = q > 0.5), then—all voters voting for the policy they personally think is best given their private information—the probability that a majority rule vote will result in the correct decision goes to 1 as the number of voters becomes large. The result is a simple example of the law of large numbers. A watershed paper by Austen-Smith and Banks (1996) raises serious questions about Condorcet’s implicit assumption that all voters will vote naively, that is, vote

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as if they were the only voter. They formally recast the CJM as a voting game and study the properties of the Nash equilibria of the game. They show that the common assumption of naive voting is generally inconsistent with equilibrium behavior. Instead, the equilibrium of the game can be quite complicated and can lead to counterintuitive and perverse results. These equilibrium voting strategies are quite sensitive to the details of the voting procedure as well. The main insight is that since optimal voting behavior follows a pivotal voter calculus,103 a voter’s equilibrium posterior over the states depends not only on his or her private signal, but also on the information implied by the event that he or she is a pivotal voter; and that information depends on the strategies of the other voters. However, the logic and the cognitive requirements of equilibrium behavior are daunting, so this raises the behavioral question of whether voters vote naively/sincerely or vote according to the equilibrium pivotal calculus. The answer has significant implications for the aggregation of information in voting rules because full information aggregation in the limit may not be a property of plausible Nash equilibria, even when it is a property of naive voting. Guarnaschelli, McKelvey, and Palfrey (2000) is the first published laboratory study of behavior in CJM voting games with information aggregation.104 The paper is based on Feddersen and Pesendorfer’s (1998) analysis of strategic voting under unanimity rule, with a default status quo. That is, outcome A occurs unless all voters (jurors) vote for B. The motivating example is the commonly used voting rule for juries in criminal trials in the United States. The defendant is convicted if and only if all jurors vote for conviction, otherwise he goes free.105 So, a corresponds to innocent, b to guilty; A corresponds to acquit and B to convict; α corresponds to a private signal indicating probably innocent and β, probably guilty. The standard justification for unanimity rule is to protect the innocent: that it reduces the probability of a “bad” error, where an innocent defendant is convicted, possibly at the expense of increasing the probability of the “less-bad” error of acquitting a guilty defendent. Feddersen and Pesendorfer’s (1998) remarkable result is that, in equilibrium, the unanimity rule in juries has the opposite effect of the intended one: Nash equilibrium may lead to a higher probability of convicting the innocent than subunanimity rules, including majority rule. In particular, it is generally not a Nash equilibrium for all voters to just follow their own signal. Put yourself in the position of a voter with an innocent signal (α), and think about how you should vote if you believe everyone else on the jury is voting according to their signal (vote A with an α signal and B with an β signal). Your vote makes a difference only when your vote is pivotal, which—because of the unanimity rule—occurs only if all other voters vote B. But that means that collectively the jury must have received n − 1 private β signals and just a single α signal (yours). Given this information, the state of the world is much more likely to be b than a, so your optimal vote is B (convict). Therefore, it is not a Nash equilibrium for everyone to vote their signal. The only way any information at all can be aggregated in a symmetric Nash equilibrium must have some fraction of voters with α signals voting for B—a mixed strategy. The strategic incentive for voters with a β signal are not adverse, so they all vote according to their signal. Hence, in equilibrium the voters will adopt strategies that (partially) cancel out the A-bias of the voting rule. Note that, according to this equilibrium logic, the adverse incentive effect to vote B with an α signal becomes stronger as n increases. Therefore, the problem is not overcome by having larger juries; on the contrary, this problem can be worse in large juries than small juries. This directly contradicts the standard jurisprudential argument both for unanimity rules and for relatively large (twelve-member) juries. Naive intuition suggests

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that raising the hurdle for conviction will reduce the chances of a false conviction. But that intuition relies on an assumption that voting behavior is unaffected by the voting rule or the jury size: voters are assumed to be nonstrategic and just vote according to their own personal signal, as if there were no other voters. Game-theoretic reasoning says the opposite: when the hurdle for conviction is raised, voters are less willing to vote to acquit. There are a number of reasons to second-guess the behavioral predictions of Nash equilibrium in this voting game. First, if legal scholars and brilliant minds like Condorcet believe voters will be sincere, then how could one expect the average voter to be smarter and realize that this simple intuitive reasoning is flawed? Second, logic requires voters to condition on hypothetical events—the event that one’s vote is pivotal. The strategic pivotal calculus of Nash equilibrium is extremely complicated, and its computation requires repeated application of Bayes’ rule, conditioning on low-probability hypothetical events (pivot probabilities), and expectations that other voters are also doing these calculations. There is abundant evidence from economics and psychology that judgements of low-probability events are flawed, that individuals update beliefs in ways that often systematically violate Bayes’ rule, and that they poorly understand how to condition probabilities on hypothetical events. Third, as it turns out these equilibria typically involve the use of mixed strategies, and laboratory data exist in other contexts indicating (1) individuals find it difficult to implement mixed strategies and (2) Nash equilibrium is often a poor predictor of behavior in games with mixedstrategy equilibria, even when the equilibrium is unique (Ochs 1995). As if three reasons were not enough to justify an experiment, there was an additional fourth reason that motivated the experiment of Guarnaschelli, McKelvey, and Palfrey (2000). Logit quantal response equilibrium and Nash equilibrium make drastically different qualitative and quantitative predictions about the effects of jury size and voting rule on the probability of correct jury decisions, especially for large elections. The limiting result about the accuracy of jury group decisions in Feddersen and Pesendorfer (1998) is a knife-edge result that depends on 100% rationality of the voters. With stochastic choice, the standard jurisprudential arguments reemerge as properties of the quantal response equilibrium: (1) majority rule leads to more false convictions than unanimity in large juries, and (2) larger unanimous juries produce fewer false convictions than smaller unanimous juries. The experimental design was 2 × 2 × 2, where the treatments varied according to (1) jury size—three or six, (2) voting rule—majority or unanimity,106 and (3) preplay communication—straw poll or no straw poll. For all treatments in the design, the two states were equally likely a priori and signal informativeness was q = 0.7. A within-subject design was employed with respect to the voting rule and the straw poll. That is, in each session of the experiment, the jury size was fixed, but subjects participated in an equal number of committee decisions under both majority and unanimity rule and with and without a straw poll. This was done by dividing each session into a sequence of four parts, with fifteen repetitions of each part with random matching. Four sessions were run, each with twelve subjects. The central finding was that voters do indeed vote strategically in juries that operate under a unanimity requirement. In the unanimity committees that operated without a straw vote, essentially all β signal voters vote for B and a large fraction of α signal voters also vote for B rather than following their signal. Moreover, the fraction of α signal voters who vote for B rather than following their signal was significantly higher in the six-person committees than in the three-person committees. The proportions are given

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TABLE 6.2: Proportion voting for B, by signal. U

Voter Signal

M

Voter Signal

n

α

β

n

α

β

3 6

0.36 0.48

0.95 0.90

3 6

0.06 0.21

0.97 0.98

TABLE 6.3: Proportion of incorrect committee decisions in state b. Unanimity

Majority

n

No Straw Vote

Straw Vote

n

No Straw Vote

Straw Vote

3 6

0.53 0.73

0.36 0.44

3 6

0.30 0.21

0.19 0.11

in left panel of Table 6.2. In contrast, under majority rule, voters without a straw poll voted their signal more than 94% of the time (right panel).107 The second finding was that the straw vote led to significantly better information aggregation under both voting rules. It is easy to show that under unanimity rule, it is an equilibrium for voters to vote sincerely in the straw-vote stage and then follow the majority outcome of the straw vote in the binding-vote stage. Nearly all the gains occur in the b state, because with a straw vote nearly all α signal voters also vote for B rather than following their signal if B won the straw vote. Table 6.3 compares the proportion of incorrect committee decisions in state b for all the treatments. In other words, the straw-vote stage converts the unanimity mechanism into what is essentially a majority voting rule. This is what was observed in the data. Voters voted their signal over 95% of the time in the first stage and followed the straw-vote majority about 85% to 90% of the time in the second binding-vote stage. Third, the predictions of QRE capture several of the main features of the data, both with respect to comparative statics and quantitatively, while many of the Nash equilibrium comparative static predictions about committee decisions fail.108 But the main takeaway from the experiment is what the data say about the three “obvious” reasons to be suspicious of the Nash equilibrium behavior. (1) Do voters follow the same naive intuition as legal scholars and great thinkers? No, it is something in between Nash equilibrium and naive play. Most voters respond strategically to the voting rule; but their response has a significant stochastic component. (2) Is the strategic reasoning too complicated for voters in the laboratory to behave according to theory? No, their behavior indicates that they understand the basic incentives, although they do not perfectly best respond. Variations in strategic behavior can be approximated by the Logit version of QRE. (3) Does the fact that equilibrium is in mixed strategies lead to problems? No. In fact, QRE assumes that behavior is inherently stochastic and accurately predicts the probability distribution of aggregate behavior. Analysis of individual behavior in these experiments uncovers a wide diversity of patterns of individual choice behavior. Aggregate behavior is consistent with the interpretation of mixed strategy equilibria (or QRE) as an “equilibrium in beliefs.” Others have investigated variations on this basic jury experiment. Ali and others (2008) conduct an experiment that does two things. First, it demonstrates the robustness

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Voter Signal

n

α

β

3 6

0.35 (382) 0.52 (616)

0.94 (338) 0.94 (464)

of the results about strategic voting of Guarnaschelli, McKelvey, and Palfrey (2000) by conducting a new experiment with the same basic environment but with much different implementation in terms of experimental protocol and procedures. Ali and others use repeated matching (standing committees) rather than random matching (ad hoc committees), use a signal informativeness of q = 23 , employ a between-subject design rather than a within-subject design, use a different computer program, with a much different interface, computerize all the randomizations,109 computerize the (much shorter) instructions, and use a different subject pool and laboratory. They do not have any straw votes and report results only for unanimity rule. The Nash equilibrium probability of voting for B given an α signal is 0.32 for n = 3 and 0.66 for n = 6. The empirical proportions voting for B in the experiment are given in Table 6.4. Ali and others (2008) also test theories of equilibrium bandwagon effects110 by observing voting behavior in committees that operate under sequential voting rule, where later voters are able to observe the votes cast by earlier voters. They provide some weak evidence of bandwagon effects, but the overall effect on voting outcomes is relatively small. The main difference is that sequential voting produces more B outcomes (i.e., unanimous verdicts) than simultaneous voting. As a result the probability of a correct decision in the a state is lower with sequential voting and the probability of a correct decision in the b state is higher. Hung and Plott (2001) also look at majority juries that vote sequentially rather than simultaneously and obtain similar results to Guarnaschelli, McKelvey, and Palfrey (2000). Goeree and Yariv (2010) successfully replicate and significantly extend Guarnaschelli, McKelvey, and Palfrey (2000). In particular, the paper explores more deeply the earlier finding that straw votes improve information aggregation in laboratory Condorcet jury games. They allow richer preplay communication111 than the simple binary message preplay communication of a straw vote, consider preference configurations that are heterogeneous, and compare voting behavior in committees operating under three different voting rules ( 95 , 79 , and 99 ). They find that their richer message space leads to much greater improvements in information aggregation than was observed in the Guarnaschelli and others’ study. Voters generally reveal their signal to all other committee members during the chat stage. The results also relate to the theoretical paper of Gerardi and Yariv (2007), which shows that if one allows for unrestricted communication, then nearly all voting rules generate the same set of equilibrium outcomes; in particular, they can lead to higher efficiency.112 Goeree and Yariv (2010) find that their three different voting rules produce very similar outcomes, suggesting that there is some deeper equilibrium selection criterion that applies to all voting rules with unrestricted communication. To the extent that these information aggregation problems are largely common-value coordination games, then efficiency

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seems like a natural selection criterion that would apply with roughly equal force to all these voting games with communication. Dickson, Hafer, and Landa (2008) explore the effect of preplay communication, or deliberation, in a three-person committee voting experiment where voters have signals about the true state of the world and preferences have both a private- and a common-value component. Incentives to communicate are more complex in this environment because the voters have different state-contingent preferences. They find that deliberation induces more information transmission than the equilibrium predictions would sugggest. This finding is similar to results of previous studies based on the Crawford-Sobel model of strategic information transmission (Dickhaut et al. 1995; Cai and Wang 2006) but in a much different setting with less-structured communication. Morton and Williams (1999, 2001) report experiments that are a hybrid of the HungPlott sequential elections and earlier experiments described earlier on multicandidate elections. Just as polls can serve as a coordination device for voters, so can sequential elections. Indeed, this is exactly the idea behind bandwagons in primary campaigns. Voters of the same party converge on the candidate who seems most likely to win in the general election (ceteris paribus). Different voters have different information, or “hunches,” about the electability of the candidates, so the question is whether this information is gradually aggregated over sequential elections. Their experiments show that voters do indeed learn from earlier results. All the preceding studies explore models where voting is costless. Following Battaglini (2005), Battaglini, Morton, and Palfrey (2008a) compare sequential and simultaneous voting in Condorcet jury games, when voting is costly and each voter chooses between voting for A or B or abstaining. In this case the efficiency question revolves around more than just information aggregation. Voting costs are also relevant. A committee’s objective is to reach the best decision at the lowest cost. The study uses three-person committees. Ties were broken randomly. There was a high-cost treatment and a low-cost treatment. All voters had the same costs, and signal informativeness was q = 0.75. Each subject participated in twenty repetitions of one of the sequential voting games (high or low cost) and twenty repetitions of one of the simultaneous voting games, with random matching. The simultaneous voting games were conducted much like in Guarneschelli and others (2000) but with the added twist of a voting cost and the opportunity to abstain. Observed turnout was higher in the low-cost treatment than the high-cost treatment, as expected. However, there were significant departures from the symmetric equilibrium. In the high-cost treatment, the observed turnout rate (32%) was significantly above equilibrium (11%). In the low-cost treatment, the observed turnout rate (61%) was significantly below equilibrium (100%).113 The equilibrium in the sequential game was quite a bit more complicated. There can be two kinds of equilibria. For sufficiently low-cost voting, the equilibrium is for the first voter to vote; the second voter votes only if he or she received a signal opposite of how the first voter voted and abstains otherwise; the third voter votes only to break a 0–0 or 1–1 tie.114 For sufficiently high cost, the first and second voters abstain and the third voter votes. Thus, with low costs, the early voters bear more of the voting costs, and with high costs, the later voters bear the voting costs, so there are opposite implications about turnout “trends” over the voting sequence as well as implications about equity. The results are qualitatively similar to the theory, in the sense that for almost all information

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sets voters abstain most of the time when that is their equilibrium action and vote most of the time otherwise. However, like the simultaneous voting game, there is quite a bit of noise in the data.115 With this in mind, the Logit QRE model was fit to the data. Fairly close fits are obtained in both the sequential and the simultaneous voting games, constraining the λ estimates to be same across cost treatments (or fitting one cost treatment using the out-of-sample estimate obtained from the opposite cost treatment). The paper also compares both the informational efficiency (probability of a correct decision) and economic efficiency (taking into account voting costs) between simultaneous and sequential voting methods.116 With respect to both kinds of efficiency, the sequential voting method is slightly more efficient but most of the differences are either not significantly different from zero or significant but small in magnitude. In both cases, as expected, there is little difference in informational efficiency and somewhat greater difference in economic efficiency. Principal Findings for Condorcet Jury Experiments 1. Most voters vote strategically in the laboratory in ways that are qualitatively similar to equilibrium models of Condorcet juries with noisy best response. 2. There are strong and significant differences in voting behavior between simultaneous voting procedures and sequential voting procedures. However, the differences in efficiency are relatively small, with sequential voting procedures somewhat more efficient, especially if voting is costly and abstention is allowed. 3. Preplay communication in the form of either straw votes or deliberation, increases efficiency, and such communication reduces or eliminates the effects of different voting rules. 5.2 The Swing Voter’s Curse The swing voter’s curse is an especially interesting application of the Condorcet jury model. If voters are differentially informed (i.e., some are better informed than others), then even when voting is costless, abstention is a relevant equilibrium phenomenon. It’s fairly easy to see why. Suppose you and your two roommates have identical preferences over movies, but it is common knowledge that only you actually know the content of two possible movies, A and B, that are playing in your local theater, and you have all decided to go out. Your roommates, with no information at all, have a prior belief equal to 0.50 that A is better. Being a democratic group, you vote on everything but anyone can abstain if they want. What is the equilibrium of the majority voting game where ties are broken randomly? You, with full information, vote for the movie you prefer, and your roommates abstain. They can’t possible gain by voting, and if one of them votes for the movie you don’t vote for, then your group goes to the wrong movie with probability 0.50. In other words, a poorly informed voter reduces his or her own utility by being pivotal. That is the simplest example of the swing voter’s curse. That was easy. Now suppose instead that your roommates share a common prior belief of 0.99 that A is better. Wouldn’t they be better off voting for A? No. The preceding argument is independent of the prior beliefs of the uninformed voters. They should still abstain. Next consider a variation on this. Suppose that one of your roommates, Ann, has different preferences and always prefers to go watch a comedy rather than any other type of movie, regardless of how corny the comedy happens to be; and suppose A is a comedy. The other roommate, Bill, has preferences just like you and wants to go to

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TABLE 6.5: Voting behavior of uninformed voters. n

A

7 9 11

0.00 0.06 0.04

π = 12 0.08 (0.00) 0.43 (0.36) 0.77 (0.76)

0.91 0.51 0.19

0.20 0.12 0.16

π = 59 0.07 (0.00) 0.35 (0.33) 0.56 (0.73)

0.73 0.53 0.28

7 9 11

B

abs

whichever movie is “better.” What is the equilibrium now? It is perhaps a bit unintuitive, but the equilibrium has you voting for the movie you “know” is better, Ann votes for A, and Bill votes for B (even though his prior belief is very strongly in favor of A). He votes for B because it ensures that you will cast the pivotal vote. This phenomenon can be called vote balancing. Feddersen and Pesendorfer (1996, 1997, 1999) are theoretical papers that explore the equilibrium properties of the swing voter’s curse and its implications in regard to patterns of abstention and information aggregation in committees and in large elections. Battaglini, Morton, and Palfrey (2010) conduct the first experimental test of this theory, which (like the preceding example) can have rather unintuitive voting strategies. That study considers committees with seven, nine, and eleven members. Seven of the voters are just like voters in the standard jury problem with identical preferences and just want to choose the better outcome, which depends on the state). In the nine-member committee, there are also two partisans, who, like Ann, prefer outcome A regardless of the state; in the eleven-member committees, there are four A-partisans. In the experiment, the partisan’s votes are automated by a computer so they always vote for A. The remaining seven human subjects then independently draw a signal. With probability 14 a signal is perfectly informative, and with probability 34 a signal is completely uninformative. Voters observe only their own signals, so they don’t know how many (if any) of the other subjects are informed. In one series, subjects all start out with a prior belief of π = 12 on state A; in the other series, the prior is π = 59 . As in the model, the information structure is common knowledge. In the seven-voter committees, the equilibrium is just like the simplest example given earlier. For both of these prior beliefs, only informed voters should vote, and all other voters should abstain. In the nine- and eleven-voter committees, the uniformed voters should balance by mixing between abstention and voting for B. In each session, the prior is fixed for the whole session, and subjects engage in thirty elections—ten each with seven, nine, or eleven voters in the committee—using a random matching protocol.117 The observed voting frequencies of uninformed voters are given in Table 6.5. Equilibrium probabilities of voting for B are in parentheses. All the comparative static predictions of the theory are supported. More partisans lead to more balancing, with less balancing if the prior state probability is biased toward the partisans. With π = 12 the results are very close to the theory. Very few uninformed voters succumb to the swing voter’s curse in this series (about 5% of votes overall). However, in the series with a biased prior, π = 59 , a nonnegligible fraction of voters

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succumb to the swing voter’s curse by voting for A. There is also a fair amount of learning, with cursed voting declining significantly with experience. In a followup study, Battaglini, Morton, and Palfrey (2008b) conduct a replication with larger committees ranging from n = 17 to n = 33, including up to twelve partisans. The results scale up fairly well, including the comparative statics on the number of partisans and the finding of 10% to 20% cursed voting behavior in the π = 59 series. One minor difference is that in one session (with twenty-one human voters) there was a surprising amount of cursed voting (around 20%), including in the elections with no partisans. However, there were only four sessions conducted in total, and no random rematching between elections, so the effective sample size is not very large. Morton and Tyran (2011) observe that there can be multiple equilibria in voting games with a swing voter’s curse for some preference and information configurations. They extend the experiments of Battaglini and others by exploring an environment where poorly informed voters are not completely uninformed—they just receive lowerquality informative signals. This can lead to multiple symmetric pure strategy equilibria. There can be an equilibrium where all voters vote and, at the same time, an equilibrium where the poorly informed voters abstain.118 If the information gap is large between high- and low-quality signals, then the latter equilibrium is more efficient, while the full-turnout equilibrium is more efficient when the information gap is small. They find significant abstention in both cases, suggesting that efficiency is not a good selection criteria in these games and also suggesting that the logic of equilibrium abstention in these asymmetric information games is intuitive and compelling even for naive subjects. A natural question arises concerning the relation between these results for the swing voter’s curse summarized before and experimental findings about the well-known winner’s curse problem that leads to overbidding in common value auctions. Like the winner’s curse in auctions, the swing voter’s curse can happen only if there is some degree of common preferences shared among some subset of voters (bidders) and if voters do not condition expected payoffs properly on the strategies of other players and low-probability hypothetical events. In the case of the common value auction, the hypothetical event is winning the auction, which is not known until after the bid is submitted. In the case of the swing voter’s curse, the hypothetical event is casting a decisive vote, which is not known until all votes have been counted and a candidate has been elected. Rational decision making in both cases requires a deep understanding of the strategic complexity of the game as well as a correct (and subtle) application of Bayes’ rule. In spite of this apparent similarity between the environments, the results reported from laboratory experiments are quite different. In the case of the swing voter’s curse, the findings are relatively consistent with the theoretical equilibrium: voters seem to “get it” and abstain (or balance against partisans) when they are poorly informed. In contrast, bidders in laboratory auctions often fail to adequately discount their bids to compensate for the winner’s curse effect. This is puzzling: Why is the winner’s curse in laboratory auctions a major behavioral effect that persists with experience, while the swing voter’s curse in elections appears to be at best a minor behavioral phenomenon that declines rapidly with experience? There are several possible answers. One conjecture has to do with learning and feedback. In the swing voter’s curse experiments, voters observe that many voters are abstaining in early rounds, so imitation could lead to convergence in the case of no partisans. Also, in the swing voter’s curse, experiments where the informed voters are perfectly informed, an uninformed voter who was pivotal and voted for the wrong candidate probably can infer that the voters who voted the other way were probably perfectly informed. In fact, these perfectly informed

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TABLE 6.6: Observed frequency of uninformed bids. All 30 Rounds Session

Treatment

1 2 3 Pooled

B = 10 B = 11 B = 11

Bid

14 0.04 0.04 0.04 0.04

B

CE

0.07 0.03 0.07 0.06

Last 15 Rounds

BNE

n

14

BC E

1B N E

n

0.89 0.93 0.89 0.90

240 240 240 720

0.03 0.03 0.04 0.04

0.01 0.01 0.00 0.01

0.96 0.95 0.96 0.95

120 120 120 360

1

voters conform to equilibrium by voting their signal virtually 100% of the time. If uninformed voters make this reasonable inference, then it is an easy next step to adapt their behavior and abstain. A second conjecture is that both the information structure and the strategy space in a typical common-value auction experiment are far more complex than in the swing voter’s curse experiments. In the auctions, the signals are virtually continuous and the joint distribution of signals and states very complicated. The strategy space is also nearly continuous. In the swing voter’s curse experiments, the strategy space is discrete, with only three possible actions, the state space and signal space are both binary, and the signals (in most cases) are perfectly informative. With this second conjecture in mind, the following experiment was designed and a few sessions conducted. The idea is to run a common-value auction experiment where the informational and strategic environments are as close as possible to the laboratory elections. In the elections reported in Battaglini, Morton, and Palfrey (BMP; 2008b, 2010), there are two states of the world, perfectly informative signals, and three possible choices. We study here a first-price common-value auction environment with nearly the same information structure: there are two states (a high common value and a low common value), perfectly informative signals, and three possible choices (bid high, bid low, bid medium). The experiment, reported in Palfrey (2012), is a seven-bidder first-price commonvalue auction. There are two possible common values, high (V = $20) and low (V = $4). It is common knowledge that these are the only two possible values, and they are equally likely. Before the auction begins, the true value is drawn by nature, and exactly three of the bidders are informed of the true value. The remaining four bidders receive receive an uninformative signal.119 The bidders then are allowed to submit one of three bids, $14, $B, or $1. There were two slightly different treatments. In one treatment, B = $10. In the second treatment, B = $11. Initially, one session of each treatment was conducted, using Caltech students as subjects, and later a second session with B = $11 was conducted to see if the results were replicated. Each session had fourteen subjects, and each subject was in thirty seven-bidder auctions, with a random matching protocol (and random assignment of informedness). The equilibrium in all cases is for informed bidders to bid $14 or $1 if the value is $20 or $4, respectively. Uninformed bidders should always bid $1. Uninformed bidders bidding $B is a cursed equilibrium strategy. Out of 540 bids by informed bidders, 539 were equilibrium bids. More surprising is that uninformed bidders quickly converged to the strategy of bidding $1. This is summarized in Table 6.6. The findings, while based on a small sample, are decisive. There is very little winner’s curse behavior in these auctions, and it completely disappears with experience. There

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is almost no difference between the two B treatments nor across the three sessions. If anything, there is less winner’s curse behavior in these auctions than there is swing voter’s curse behavior in the BMP elections. These results suggest that it would be useful to explore more-complex information environments in the committee setting in order to dig more deeply into the swing voter’s curse phenomenon. If the conjecture in this paper about the connections between complexity and cursedness is valid, then it should not be too difficult to design a swing voter’s curse experiment where cursed behavior is prevalent. On the theoretical side, it would seem useful to explore and develop models that connect some formal measures of complexity or transparency of games to the degree to which economic and political agents are subject to behavioral limitations such as cursedness, strategic unsophistication, and noisy best response. Principal Findings for the Swing Voter’s Curse 1. Voters with relatively poor information abstain in ways that are largely consistent with swing voter’s curse theory. That is, for the most part voters avoid the curse by abstaining. 2. There is some cursed voting behavior (10%–20%) if the uninformed voters’ prior on the state of the world is biased for one of the states. 3. Uninformed voters balance, with a significant fraction of them voting against the partisan side in the election. This fraction increases in the number of partisans. 4. The results scale up to larger electorates.

6 VOTING MECHANISMS THAT REFLECT PREFERENCE INTENSITY Most of the classic literature in voting theory and social choice theory employs ordinal models of preference in one dimension or with a finite number of alternatives or consider purely redistributive politics, as in the BF model. Spatial models typically assume Euclidean preferences, which, in two dimensions, implies that there is no difference in preference intensities across issues.120 This lack of emphasis on preference intensity, or “willingness to pay,” stands in stark contrast to the classic literature on public goods, where intensities of preference for a public good play a fundamental role; in the standard public goods literature intensities are often captured by marginal rates of substitution between public goods and a numeraire private good. In the absence of different preference intensities across issues, there are some compelling arguments for using majority-rule issue-by-issue voting. In particular, majority rule is the unique method for choosing over binary issues in a way that simultaneously respects anonymity of the voters, is neutral with respect to the alternatives being voted on, and is positively responsive to preferences. However, with differing preference intensities across issues (as represented by different marginal rates of substitution between the public decisions and a numeraire private good, or “private valuations” as in auction theory), it is easy to find examples where majority rule will lead to highly inefficient public decisions. A typical example of inefficiency might have three voters and two binary issues. In issue one, the alternatives are {x1 , y1 }, and in issue two the alternatives are {x2 , y2 }. Suppose the private valuations of voters are as in Table 6.7. The majority-rule outcomes are y1 for issue 1 and y2 for issue 2. However, the efficient outcome would have outcome x1 for issue 1 and x2 for issue 2. Majority-rule issue-by-issue voting clearly fails to lead to an efficient decision. Are there better voting

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TABLE 6.7: Voter preferences on two binary issues.

Voter 1 Voter 2 Voter 3

x1

y1

x2

y2

15 0 0

0 8 4

5 0 0

0 2 2

methods that circumvent this problem of the “tyranny of the majority”?121 One might propose to allow for vote trading, but voters 2 and 3 always win on both issues, so there are no mutual gains from vote trading. One might also propose to offer an “omnibus” bill that combines the two issues. For example, one could vote for the efficient combined outcome x1 x2 against the complementary alternative y1 y2 . But this doesn’t work because voters 2 and 3 both prefer y1 y2 to x1 x2 , which would actually result in the least efficient outcome on both issues. In fact, the issue by issue majority rule outcome, y1 y2 is a Condorcet winner, or majority-rule core, and hence a very stable outcome with respect to simple majoritarian mechanisms. The rest of this section reviews the experimental findings based on various theoretical voting mechanisms that have been proposed to ameliorate the preference-intensity problem inherent in majority rule (or any other simple voting rule based solely on ordinal preferences). The basic approach is along the lines of mechanism design theory, and hence the main questions—and the questions most intently focused on in the laboratory experiments—concern the welfare gains of these alternative voting mechanisms as compared to simple issue-by-issue majority rule. Under what conditions does an alternative voting scheme lead to better or worse outcomes than majority rule, from a utilitarian criterion? Is the kind of strategic behavior predicted by equilibrium theories of behavior in these voting games similar to what is observed in the experiments? Do some of these alternative schemes perform better than others? Are the findings robust with respect to environments and institutional details? 6.1 Mechanisms Where a Budget of Votes Can Be Allocated Across Issues Storable Votes A mechanism called storable votes was proposed by Casella (2005, 2011). A committee of voters faces an upcoming sequence of votes on T binary issues. In the simplest version of it, each voter is endowed with a total of T votes, one for each issue, but a voter can choose to abstain on issue t and save the vote for use in a later issue. Thus, for example, in the case of T = 2 a voter can cast one or zero votes on issue 1, and as a result have one or two votes for issue 2. One solves for subgame perfect equilibria in stage-undominated strategies (i.e., any votes cast on an issue are cast for the voter’s preferred alternative). Referring to the preceding example, there is an equilibrium where voter 1 votes twice on issue 1 and voters 2 and 3 each mix between voting twice on issue 1 and voting once on each issue. Even though the outcome is not fully efficient—a probability distribution over outcomes—it improves over issue-by-issue majority rule.122 The main theoretical result is that storable votes typically improves over simple majority voting. Casella, Gelman, and Palfrey (2006) study a variation123 of this voting mechanism using a laboratory experiment for T = 2, 3 and committee sizes n = 2, 3, 6. Each session consisted of between 8 and 21 subjects playing 30 repetitions of the storable votes

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mechanism using a random matching protocol. Valuations for each voter’s favored outcome on an issue were independently and uniformly distributed between 1 and 100. The direction of preference of each voter (i.e., which outcome on an issue was a voter’s favored outcome) was determined by a computerized coin toss. This was explained carefully to the voters. At the beginning of period t each voter was privately informed of his or her own valuation and direction of preference for issue t but were not yet informed of a valuation or directional preference for future periods. Each voter’s endowment of bonus votes was fixed at B = T . There were several findings. The main finding was that the efficiency improvements predicted by the theory were largely borne out in the data. A second finding was that the voting strategies of subjects were substantially (and significantly) different from the equilibrium strategies. For example, in the case T = 2, equilibrium strategies always have voters using all their bonus votes on one single issue rather than splitting. However, splitting of bonus votes was commonly observed. On the other hand, subjects did generally use monotone strategies, in the sense that the number of bonus votes used on the first issue was an increasing function of the voter’s valuation on that issue. The paper considers a range of stochastic choice models and shows that among these models, the logit QRE model organizes the data rather well. Casella (2011a) investigates a variation of the model where an agenda setter can choose the order that issues are voted on. There exist equilibria where the agenda setter indeed has proposer power in the sense of getting a higher expected payoff than if the agenda were set randomly. For the example with T = 2, this is done by first conducting a vote on the issue for which the setter has the higher valuation. This signals to the other voters that the agenda setter is going to use his or her bonus votes for the first issue, which has a preemptive effect on other voters. Theoretically there are still overall welfare gains compared to simple issue-by-issue majority voting. The experiments (using n = 3, 4 and T = 3 and a random matching protocol) confirm the welfare gains, thus replicating the findings of Casella, Gelman, and Palfrey (2006) in a more complex setting. However, there is no measurable proposer advantage. The setter is unsuccessful in exploiting his control of the agenda order. One of the supposed advantages of storable votes, besides producing some efficiency gains, is overcoming the problem of the tyranny of the majority. This has been a topic of considerable importance in democratic theory, since the legitimacy of majority rule democratic procedures may be eroded away if minority political factions always fail to have an effective voice, even on issues where their preferences are more intense than the majority. Storable votes make it feasible for minority factions to exercise power on at least some issues by concentrating their votes on those issues most important to them.124 Casella, Palfrey, and Riezman (2008) investigate the question of whether minorities are more successful with a storable votes system than simple majority rule and how this can affect efficiency. Their experiment is another variation on Casella, Gelman, and Palfrey (2006), having different numbers of members with preferences for or against proposals. To reflect the importance of systematic minorities, the smaller faction was always in favor of outcome at and the larger faction was always in favor of outcome bt . Thus, under simple majority rule, the outcome would always be bt for all t. The experiment varied a number of factors, such as the correlation of valuations and the ability of groups to communicate prior to voting. The main finding is that storable votes does indeed help minorities win on those issues where they have the highest valuation. This effect is magnified when their valuations are correlated. The second finding is that this increase in minority representation comes at essentially no efficiency loss. The

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third finding is that the ability coordinate via direct communication had relatively little effect on outcomes. Qualitative Voting and Linking Decisions The storable votes mechanism is but one example of a more general phenomenon that Jackson and Sonnenschein (2007) refer to as linking decisions. That is, one can link the outcomes across issues in such a way that voters who are successful on one issue will be less likely to be successful on other issues. Such mechanisms create incentives for voters to adopt strategies that will be more likely to lead to successful outcomes on those issues they care most about. In the storable votes mechanism, this is completely intuitive: by using up one’s bonus votes on issue 1, it reduces the likelihood of winning on issue 2. Jackson and Sonnenschein consider a more general class of mechanisms where voters can cast continuous votes (similar to bids) for or against each proposal, subject to a budget constraint on total votes. However, voters are effectively constrained so that the frequency distribution of votes they cast across the issues is tied to the probability distribution of their valuations. Thus, for example, if valuations were drawn from a uniform distribution, then a voter would have to cast votes across the issues that approximated a uniform distribution. Such a mechanism has strong incentive compatibility properties if there is a large number of issues and hence leads to efficient decisions in the limit as the number of issues becomes infinite. Hortala-Vallve and Llorente-Saguer (2010) conduct an experiment to explore a mechanism that links a finite number, N, of issues in a committee of two members by endowing each member of the committee with a budget of six votes to allocate across the issues. Voting takes place simultaneously on all N issues, using majority vote with ties broken randomly.125 They run treatments of N = 2, 3, 6. The two members have opposite preferences but can differ in their intensities (valuations) on each issue, as in the storable votes model. One is always in favor and one is always opposed in all issues. Intensities are independent draws from a uniform distribution over a coarse grid ranging from 7 to 11 possible values. Voting takes place after each member has observed his or her own intensities for all issues but none of the intensities of the other voters. Thus, it is essentially the same as the storable votes experiment, except all valuations are announced at the beginning and all voting takes place simultaneously. The unique Nash equilibrium predicts efficiency to be above 80% in all treatments and to be increasing in the number of issues. Both these equilibrium properties are observed in the data. However, as in the storable votes experiments, subjects generally do not use equilibrium strategies, although strategies are nearly always (96%) weakly monotone in valuations. That is, more votes are allocated to higher-intensity issues. As is the case with storable votes, the mechanism is somewhat robust in the sense that significant efficiency improvement results simply from the use of monotone strategies, even if they are not using equilibrium strategies. Hortala-Vallve, Llorente-Saguer, and Nagel (2012) compare the performance of the preceding mechanism to open negotiation with unlimited communication and a deadline and investigate how the comparative performance depends on the information structure. Under negotiation, an agreement requires a vector of decisions, one for each issue.126 Valuations are drawn uniformly from a grid of 10 valuations, {50, 100, 150, . . . , 500} subject to the constraint that valuations across all issues for a voter sum to 600. Thus there is dependence across issues in the draws for a given voter but independence across voters. In case the deadline is reached without agreement, both voters receive 300, the expected payment if there were to be a coin toss on each issue. In the voting mechanism, ties result in each voter receiving half their valuation.

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As in the earlier experiment, they consider N = 2, 3, 6. They find an interesting interaction effect between information conditions and mechanism performance. With complete information the bargaining mechanism produces more efficiency gains, but the comparison is reversed with incomplete information. Engelmann and Grimm (2012) also conduct an experiment using a simplified version of the linking mechanism. Subjects are assigned valuations (intensities) across forty issues and are paired (N = 2). The issues are decided in sequence. There is no repetition of the task. The two members of a pair have opposite directions of preference on a binary issues. Valuations can take on only two values, high or low, which are determined randomly and independently across issues. For each issue, subjects are asked to say whether their valuation is high or low. If they make different announcements, then the social decision is the one preferred by the agent with the high valuation. If they both make the same announcement, the social decision is determined by a coin flip. Finally— and this is the key—subjects are allowed to announce high valuations on only twenty of the forty issues.127 It is an equilibrium in this game to announce truthfully unless one has high valuations on more than twenty issues (in which case it is an equilibrium to randomly select twenty of those issues to announce high). Theoretically, efficiency should be almost perfect, in contrast to simple majority rule, where there would be a tie in each period, so efficiency is 50%. They contrast this with a mechanism that is essentially equivalent to simple majority rule with a random tie break. The findings track the theoretical predictions. In the (majority-rule) treatment with no constraint on high announcements, subjects announce high nearly all the time. In the mechanism that links decisions by constraining high announcements, subjects honestly report their intensities about 90% of the time. Principal Findings for Mechanisms Where Voters Have Multiple Votes to Distribute Across Issues 1. Efficiency is generally higher than simple majority rule, as predicted. 2. Voting strategies are monotone: voters use more of their budget on high-valuation issues, but the response is smoother than predicted by theory. 6.2 Vote Trading and Vote Markets At least since Buchanan and Tullock (1962), scholars in political science have conjectured that having a market for votes could potentially lead to more efficient decision making in committees, drawing an analogy with the first welfare theorem of general equilibrium theory. Two different models of a market for votes have been studied. The first model, usually called vote trading, or logrolling, is a model of pure exchange. The second model is in the Marshallian tradition, where votes are traded against a numeraire private good commodity, or money. Vote Trading and Logrolling With logrolling, or vote trading, a committee member who feels strongly about issue 1 can trade his or her vote on issue 2 to another voter who feels strongly about issue 2. If these voters would otherwise be pivotal on these two issues, they have clear incentives to make such a trade. This is essentially what is mimicked in the storable votes mechanism, but the mechanisms are different, so equilibrium outcomes may be different. Riker and Brams (1973) develop a noncooperative game model of vote trading and show that in some cases vote trading can have negative efficiency consequences because of externalities. Indeed the two voters who trade their

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TABLE 6.8: Voter valuations for a nonexistence example. Voter

X

Y

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0 0 30

votes will obviously have made a mutually beneficial exchange in equilibrium, but this can impose costs on voters who were not involved in the trade. They construct examples illustrating how the external costs can easily outweigh the benefits to the vote traders. McKelvey and Ordeshook (1980) conduct an experiment to see whether vote trading leads to higher or lower efficiency than the outcome that would arise under simple issue-by-issue majority rule without vote trading. They examine three-person and five-person committees and compare outcomes where binding bilateral commitments are possible to outcomes under more-open committee-bargaining protocols more along the lines of the unstructured committee-bargaining experiments described earlier in this survey.128 With binding bilateral commitments, they find some support for the Riker-Brams hypothesis that permitting vote trading can lead to inefficient allocations. However, if agreements to trade votes are not binding and the committee of the whole has prevote discussions, then this kind of inefficient logrolling is just not possible. Since the latter allows for essentially costless coalition formation of more than two members, bilateral attempts to reach deals that are harmful to the group as a whole are undermined. As a result, cooperative game-theoretic solution concepts organize the data from the open-bargaining experiments without binding vote-trades much better than the noncooperative vote-trading model. Markets for Votes A market for votes can lead to more efficient outcomes, even in the case where there is only one binary issue. In particular, if the minority coalition in favor of a proposal has more intense preferences than the majority coalition that opposes the proposal, then members of the minority would be willing to pay members of the majority to vote for the proposal in such a way that all members of the committee are better off. One possible way to achieve this is to allow members of the committee to openly trade their votes for money. The idea obviously extends to multiple issues as well, and the natural model to apply is general competitive equilibrium, where money is modeled as a numeraire perfectly divisible private good commodity and utility is additive across issue valuations and money. The difficulty with this approach is that the market for votes is somewhat pathological, for a variety of technical reasons. It is a market with complications, including externalities, indivisibilities, and public goods, and the outcomes respond to vote allocations in discontinuous ways. Furthermore, votes have no intrinsic value at all and have only indirect value if a voter is pivotal. As a result, competitive equilibrium as one usually defines it fails to exist. The nonexistence problem is illustrated by the following simple example from Casella, Llorente-Saguer, and Palfrey (2012). Suppose a committee deciding on a binary decision (X or Y) under majority rule has three voters, 1, 2, and 3. Voter valuations are given in Table 6.8. The majority rule outcome without a market for votes is X, but the efficient decision is Y. What would a competitive equilibrium look like? It would be a price p and demands

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9, LT 600

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4th Market Eq price

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0 0

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240 360 480 Time in a match (in seconds)

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Figure 6.15: Price dynamics in a market for votes. Source: Casella et al. (2012).

(x1 , x2 , x3 ) such that xi is an integer greater than or equal to −1 and demands sum to zero. At any positive price, voter 3 demands at most one vote: Any positive price supporting a vote allocation where either side has more than two votes cannot be an equilibrium; one vote would be redundant and so at any positive price there would be excess supply. Voter 3 could buy 1’s vote at a price of 11. But again the market will not clear: Voter 2’s vote is now worth nothing and therefore 2 would be willing to sell it for 11. In fact, any positive price supporting 3’s purchase of one vote cannot be an equilibrium: the losing vote is worthless and would put up for sale at any positive price. But a price of zero cannot be an equilibrium either: at zero price, 3 always demands a vote, but 1 and 2 will not sell and there is excess demand. Finally, any positive price supporting no trade cannot be an equilibrium: if the price is at least as high as 3’s high valuation, both 1 and 2 prefer to sell, and again there is excess supply; if the price is lower than 3’s valuation, 3 prefers to buy and there is excess demand. Casella, Llorente-Saguer, and Palfrey (2012) define an ex ante competitive equilibrium for a market for votes like this one and show by construction that a nontrivial equilibrium exists. The equilibrium always results in dictatorship if there is any trade at all. Consequently, the market for votes generates welfare losses, relative to simple majority voting, if the committee is large enough or the distribution of values are not highly skewed. They test the theoretical implications by implementing a competitive vote market in the laboratory using a continuous open-book multi-unit double auction. The experiment uses committees of sizes 5 and 9, and each committee engages in competitive markets for votes under four different distributions of valuations. Following standard laboratory market protocol, each schedule of valuations is repeated independently for multiple repetitions to allow for price discovery and convergence. A total of twenty markets were conducted for each session (five repetitions of each of the four valuation schedules). They have three main findings. The first finding is that prices begin above the competitive equilibrium and decline over time to a level above the risk neutral competitive equilibrium price but close to or within the range of competitive equilibrium with risk-averse voters. Estimates of asymptotic price convergence fail to reject the competitive pricing model in six out of eight treatments and reject it marginally in the remaining two treatments. Figure 6.15

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shows the price dynamics for one of the valuation schedules in four different sessions. The equilibrium price under risk neutrality for the markets in the figure is 50, and the equilibrium range with risk aversion is 50–100. The prices labeled as Market 1 consist of completely inexperienced traders, while Market 4 traders had the most experience. Second, in smaller committees, dictatorship resulted between 80% and 100% of the time when traders were experienced. In larger committees, where the purchase of four votes is required for dictatorship, the frequency of dictatorship was significantly lower but increased with experience. Third, the welfare predictions of the theory were borne out in the data. The difference in efficiency between vote markets compared to majority rule without vote trading had the correct sign for all treatments. Casella, Palfrey, and Turban (CPT; 2014) investigate several related questions about markets for votes but with some important differences in both the approach and the motivation. First, the informational conditions are different; in Casella, Llorente-Saguer, and Palfrey the direction of preference (i.e., whether a committee member would vote for X or Y) was private information, and the direction of preference was independently drawn with equal probability for each member. In CPT, each member’s direction of preference was common knowledge. The valuations were drawn independently from a uniform distribution, and this distribution was also common knowledge.129 Second, the vote markets in CPT were implemented as one-sided continuous openbook auctions, where only bids to buy could be submitted; in Casella, Llorente-Saguer, and Palfrey (2012) markets were implemented as double-sided continuous open-book auctions where both bids and offers could be submitted. Third, CPT was motivated by questions about how vote markets affect the tradeoff between minority voice (i.e., the probability that an intense minority can win) and efficiency (as in Casella 2011b), and the extent to which this tradeoff depended on the ability of the members of each side to coordinate their actions. Coordination was modeled as a two-player game between party leaders, which reduces the problem theoretically to a bargaining game similar to Myerson and Satterthwaite (1983) or Cramton, Gibbons, and Klemperer (1987). The theoretical Bayesian equilibrium was derived for these games. For the multiplayer vote markets without coordination through party leaders, the ex ante competitive equilibrium solution was the benchmark used for predictions about behavior in the experiment. The theory has strong predictions. In both cases (with or without coordination), trading falls short of full efficiency, but for opposite reasons: With coordination through party leaders, the minority wins too rarely; with a decentralized market in the absences of party leaders to coordinate trades, the minority wins too often. As a result, with party leaders, vote trading improves over no trade; with market trades, vote trading can be welfare reducing. These basic properties are satisfied by all experimental sessions. As in Casella, Llorente-Saguer, and Palfrey (2012), the data show some evidence of overpricing relative to equilibrium prices. Principal Findings for Majority-rule Committees with Vote Markets 1. Transaction prices for votes are generally higher than the risk neutral competitive equilibrium price but converge downward to a range consistent with equilibrium pricing with risk-averse voters. 2. Dictatorship outcomes are observed more than half the time, and such outcomes increased with experience and decreased with committee size.

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3. Decentralized markets for votes, or vote trading, can cause significant efficiency losses in a way that is consistent with the equilibrium model. Inefficiencies are greater in larger committees and in committees where the distribution of values is skewed toward higher values. 4. If vote trading is coordinated through party leaders, it generally leads to efficiency gains compared to no vote trading but falls short of full ex post efficiency.

7 WHERE DO WE GO FROM HERE? The basic findings from these various classes of political science experiments are summarized at the end of each section. Therefore, rather than resummarizing, this section will provide some discussion that points to some possible promising lines of new research in each of these areas and a discussion of open theoretical questions and what sort of experiments might be especially informative. What is on the horizon in the coming decade of laboratory research in political economy? First, one rather obvious observation. Using history as a guide, laboratory experiments in political economy will follow the current trends in theory. Thus, for example, new experiments relating to the design of optimal voting procedures in committees are a good bet, since there has been a flurry of theoretical research on this recently. In fact, we are beginning to see some experiments along this line, such as HortalaVallve and Llorente-Saguer (2010), Casella, Gelman, and Palfrey (2006) and Casella, Palfrey, and Riezman (2008), which explore the behavior of laboratory committees using novel voting methods that allow members to express strength of preference. The research on deliberation and information transmission in committees with conflicting preferences (e.g., Austen-Smith and Feddersen 2005; Meirowitz 2004) suggest a wave of experiments that would be a hybrid of the early committee experiments and the more recent experiments on information aggregation in juries. Dickson, Hafer, and Landa (2008) is an example of recent work along these lines. Questions of information aggregation in elections with more than two candidates is another promising area of research that is just starting to be investigated, both theoretically and in the laboratory (Bouton, Castanheira, and Llorente-Saguer 2012). A fourth set of experiments is suggested by theoretical models of endogenous candidate entry. These could blend insights from the earlier experiments on candidate spatial competition and more recent experiments on entry and coordination in abstract games. To date there have been only two experiments130 that investigate citizen-candidate models of political competition and none that explore other models of competition where entry and candidate policy preferences are important factors. Such experiments are surely on the horizon. A second, less-obvious observation is that the line between political science theorytesting experiments and experiments in economics and game theory has become very blurred. Accordingly, many of the recent developments and exciting frontiers in laboratory experiments in economics similarly represent exciting new frontiers of research in political science experimentation. The influence of behavioral models in economics that relax the classical model of perfect rationality has been felt in the political science community as well.131 Similarly, the questions in which political scientists are interested and basic game-theoretic models overlap significantly with the kinds of questions and models explored by economists in the laboratory. The last example (competitive markets for votes) is one obvious example. But more to the point, political scientists are deeply interested in theories of free riding (e.g., Olson 1965;

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Ostrom 1990), cooperation in repeated games (Axelrod 1984), coordination problems (Banks and Calvert 1992), contests and all pay auctions (Tullock 1980) and other such problems that are at the heart of pure and applied game theory. Thus, what many social scientists, or at least economists, automatically think of as “economics experiments” (just look at the title of this volume)—voluntary contribution to public goods, bargaining games, coordination games, repeated games, reciprocity in trust games, the dictator game, and so forth—address central questions in theoretical political science that are of significant interest to political scientists in all three main substantive fields of the discipline: American politics, comparative politics, and international relations. This brings us full circle to the dilemma faced at the start of this essay: how to define political economy experiments? This essay limited the scope of that broad swath of research out of necessity. Political scientists should be and will be interested in many of the other chapters of this handbook. While some of the most exciting experimental research in political economy focuses, like this chapter, on voting, committees, and elections, the body of laboratory research in game theory and choice behavior that shares the interest of modern political scientists and economists alike resides in an important and even larger wing of the library of political economy experimentation.

ACKNOWLEDGMENTS The financial support of the National Science Foundation and the Gordon and Betty Moore Foundation is gratefully acknowledged. I wish to thank many coauthors and colleagues for sharing their insights about laboratory experimentation in political science and game theory. John Kagel, Aniol Llorente-Saguer, Rebecca Morton, Kirill Pogorelskiy, and Rick Wilson provided many helpful comments and advice on earlier drafts of the survey. I am especially indebted to Richard McKelvey, Charles Plott, and Howard Rosenthal, who were instrumental in shaping my own research in this area. None of them are responsible for any shortcomings in the final product. Parts of this chapter expand on material from previous surveys and lectures by the author.

NOTES 1. 2. 3. 4. 5. 6. 7. 8. 9. 10. 11.

http://en.wikipedia.org/wiki/Political_economy. November 18, 2013. See Alt and Shepsle (1990). It is also the title of a monograph series published by Routledge. http://www.cambridge.org/us/catalogue/print.asp?isbn=9780521572156&print=y. This includes work by the recent Nobel prize winning political scientist Eleanor Ostrom. An exception is the chapter in the previous edition, concerning individual choice experiments (Camerer 1995). This may be changing somewhat in laboratory experiments, as experimenters attempt to scale up the minieconomies and minipolities being studied. A fourth feature of experiments in the economics tradition is the absence of deception, which is also generally the case in incentivized political science experiments. See, for example, Plott and Smith (1978). The most recent edition of Robert’s Rules of Order (Roberts, Honemann, and Balch 2011) rambles on for more than 800 dense pages. Robert’s Rules for Dummies (Jennings 2004) is 360 pages long. Many of these solution concepts came from cooperative game theory—for example, the bargaining set and the von Neumann Morgenstern solution. In the actual experiments, the outcome space is given by a finite grid of points on the plane.

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Chapter 6 12. There also some some secondary treatment variations regarding payoff magnitudes and communication limitations. 13. There are two C points because it depends on the order. 14. The quadrilateral in the series 3 figure indicates the min-max set for that preference configuration. These points can be defeated only by a minimum winning coalition of three voters. All other points can be defeated by even larger coalitions. 15. In series 1 committees, only seven out of forty committee outcomes were exactly at the core point. The frequency of core outcomes did not depend on the secondary treatment variables explored in Series 1: communication and payoff magnitude. However, the variance of outcomes was much lower in the highpayoff commitees. 16. Fiorina and Plott (1978) and later studies suggest alternative hypotheses that are suggestive of a behavioral model (such as fairness). 17. In spite of the earlier publication date, the experiments reported in Berl et al. (1976) were motivated by an early version of Fiorina and Plott (1978). 18. With issue-by-issue voting, a new alternative can alter the status quo on only one dimension. 19. Plott (1991) replicates the FP results for committees with between twenty-three and forty-five members. 20. McKelvey and Ordeshook (1981) also find evidence that core selection can depends on other details of the preference profile. 21. The voting agenda procedure in their voting experiment was constrained to a specific, well-defined multistage game, in contrast to the less-structured committee protocols used in most other experiments in this section. 22. Ordeshook and Winer (1980) conduct experiments with weighted voting and find results that are broadly supportive of the competitive solution. 23. Some related findings are reported in Miller and Oppenheimer (1982). 24. A number of subsequent studies have shown further evidence for the cardinality principle. For example, Herzberg and Wilson (1991) find that agenda access costs affect both the outcomes and the agenda path to these outcomes in majority rule committees with spatial preferences, both with and without a core. See also Eavey (1991) and Grelak and Koford (1997). 25. A more recent reexamination of these older committee experiments shows that the uncovered set, which is purely ordinal, organizes the data quite well across a broad set of experiments, in the sense that a large percentage of observations are contained in the uncovered set (Bianco et al. 2006). However, in many cases without a core, the uncovered set is a large subset of the Pareto optimal outcomes and, as such, makes rather nebulous predictions. For environments where a unique core outcome exists, the hit rate is quite small and is affected by order-preserving payoff transformations. 26. Obviously, this basic idea extends in a straightforward way to far more general environments, for example, discrete or multidimensional issue spaces, voting rules other than majority rule, and multistage political process (e.g., veto players, bicameral voting bodies, and so forth). Many such institutional features can be brought into the model under the general framework of structure induced equilibrium, an important insight and concept introduced by Shepsle and Weingast (1981). One can view the RomerRosenthal model as an early example of structure induced equilibrium. 27. Like the ultimatum game, since there are a discrete number of alternatives, there is also an equilibrium where the median voter receives a minimum positive surplus relative to the status quo. 28. This latter finding is similar to results reported in Isaac and Plott (1978) on the effect of a closed rule (i.e. only one proposal). 29. The closest to this are the multilateral bargaining experiments with voting, discussed later. 30. The author attributes this partially to his design, which allowed for repeated game effects. Still, he finds the main comparative static effect for his design, with more extreme setters proposing more extreme policies. 31. Farquharson (1969) was the first to study general properties of sophisticated voting over fixed agendas. Voters are assumed to have complete information about the preference orderings of all the voters. With incomplete information, the equilibrium analysis is much different (Ordeshook and Palfrey 1988). 32. A Condorcet loser is an alternative that is defeated in a pairwise vote with any of the other alternatives. 33. This was in part due to the presence of incomplete information in these experiments. 34. The authors also identify another deviation from their model predictions. Their model tends to underpredict the margin of victory. 35. After the decision, the authors sent out a questionnaire to get more-complete preference information from the members. 36. The target outcome coincided with the ideal point of the authors, as explained in the article.

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37. Specifically, the agendas are all binary amendment voting procedures, subjects are given the ordinal preferences of the computerized voters, and they are told that the computerized voter will vote sincerely at every stage. 38. Subjects are allowed extensive practice in an unpaid agenda game, which they can repeat as many times as they wish. On average, each subject practices the task approximately five times, and they find no correlation between the number of practices by a subject and their tendency to vote sophisticatedly. 39. See Roth (1995) for a discussion of several of these studies. 40. See, for example, the centipede game study by McKelvey and Palfrey (1992) and subsequent studies of that game. Morton (2007) has an insightful discussion about why the centipede game is important for political science, particularly as it relates to legislative bargaining. 41. The findings about convergence and learning are mixed. See, for example, Nagel and Tang (1998). Ponti’s (2000) theoretical adaptive learning model that generates cyclic dynamics in centipede games offers one possible explanation for these mixed findings. 42. Learning through repetition is also facilitated by their design, where the distribution of preference orders was fixed for all ten rounds; only the assignments of preferences changed. 43. The likelihood voters vote sophisticatedly is also higher in the pubic information treatment than the private information treatment, but significance (11%) fails conventional tests. 44. There are some extensions of this where the setter can have a second shot if the first proposal fails. 45. This does not reduce to exactly the equilibrium of the Rubinstein bargaining game if n = 2 and the voting rule is strict majority rule. The difference is due to the fact that in the standard Rubinstein game, the proposers alternate rather than being chosen at random. 46. This finding is similar to the phenomenon of incomplete rent extraction in bargaining games with side payments and in the Eavey-Miller experiment. 47. Rietz (1993) studies the use of the risk-neutralizing lottery procedure in the context of first-price auctions. See also Cox and Oaxaca (1995) and Walker et al. (1990). 48. The experiments reported in Diermeier and Morton (2005) were conducted around the same time, perhaps slightly earlier. They employed a different design and explored somewhat different questions. See the following. 49. In each session, subjects repeated the task fifteen times. There were exactly five subjects in each session, so these were “repeated-repeated games.” To mitigate supergame effects, subject ID numbers were relabeled after each election was finished (i.e., a proposal passed). Subjects received payment for a randomly selected four out of the fifteen elections. Sessions were conducted manually using a blackboard and pencil and paper, rather than computers. 50. In the baseline treatment, Gamson’s law predicts an equal split between the two coalition members. 51. Fréchette, Kagel, and Morelli (2005b) also run a DB treatment and report similar findings. 52. These delay rates were higher than was observed in the three-voter BF bargaining games reported in Fréchette, Kagel, and Morelli (2005a) and lower than the three-person DB committees with no discounting in Fréchette et al. Experience also significantly reduced delay in the three-voter games. 53. These experiments had no discounting built into the payoffs, so there is no direct efficiency loss from delay. However, if subjects’ time is valuable, then these delays did create inefficiencies. 54. Unfortunately, for the allocation data analysis, a large chunk of the data is discarded because only passed allocations with minimum winning coalitions are considered. 55. Their main finding is very high rejection rates in early rounds, compared to infinite horizon bargaining experiments. 56. See also Hsu, Yang, and Yang (2008). They are particularly close to the experimental studies of n-person ultimatum games. See, for example, Guth and Van Damme (1998), Bolton and Ockenfels (2000), Knez and Camerer (1995), and Kagel and Wolfe (2001). 57. In most sessions, the task was repeated with random matching for twelve repetitions to allow for learning. 58. Quantal response equilibrium relaxes the best response assumption of Nash equilibrium with noisy best response but retains the assumption of rational expectations. See McKelvey and Palfrey (1995, 1998) and Goeree, Holt, and Palfrey (2005). It will be discussed in more detail in Section 4. 59. Christensen (2010) extends the design of this experiment by allowing for heterogeneity of public good preferences. 60. In the experiment, the “dollar” was divisible into sixty pieces. If anything, the grid used in the laboratory version was finer than necessary: over 90% of proposals were for allocations that were divisible by five. 61. The Markov perfect equilibrium pins down predictions in these games. The entire set of subgame perfect equilibria is, of course, much larger, following folk theorem types of arguments. In fact, the efficient path can even be supported in a subgame perfect equilibrium for large-enough discount factors, including the parameters used in the experiments. The formal argument is in Battaglini, Nunnari, and Palfrey (2012).

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Chapter 6 62. The efficient level of investment required investing 100% of the endowment in all of the first ten periods. 63. There were five voters in a two-dimensional space, with Euclidean preferences. Voter ideal points were the same as in some of their committee experiments. 64. McKelvey and Ordeshook (1982) also include results from a series of elections with similar procedures but where a Condorcet winner did not exist. In this case, there is no pure-strategy equilibrium. They find that the candidate locations converge to a central area in the Pareto set and conjecture that behavior is close to the mixed-strategy equilibrium of the game. 65. There were also some three-candidate elections, which are discussed later in this survey. 66. Voters also are assumed to know approximately where they stand relative to rest of the electorate on a left-right scale. 67. This is done by having the active candidate investing in effort before knowing his or her own quality level. This produces a signal equal to the sum of the effort choice and his or her realized quality level. The signal is then revealed to a subset of the voters. The motivation behind this signal structure is that the active candidate is an incumbent coming up for reelection, and the signal is some measure of his or her performance in office during his first term. 68. In a related study, Lupia (1994) investigates a different mechanism for information revelation in direct-legislation elections. His experiment demonstrates that when incompletely informed voters have information about the incentives of the author of ballot initiatives, they can use this information to increase the likelihood they cast the same votes they would have cast had they possessed perfect information about initiative. 69. See Key (1966) and Fiorina (1978). 70. The latter article also summarizes results from the experiments on contemporaneous information such as poll results or endorsements. 71. Of course, these experiments explore relatively simple environments and focus only on the main driving force of candidate competition. Future research will need to address the role of other factors such as voter turnout, campaign contributions, advertising, the role of parties and primaries, valence dimensions, and so forth. 72. For example the alternatives were labeled Orange (A), Green (B), and Blue (C) to avoid alphabetical order as a coordinating device. 73. An exception is Forsythe et al. (1996), where voting groups were reassigned only after every eight elections. 74. The BC rule requires voters to rank the candidates from most preferred to least preferred. The candidate with the highest average ranking wins. AV is similar to the plurality voting rule, except voters are permitted to vote for more than one candidate. The candidate with the most votes wins. 75. On the other hand, it seems harder to rationalize the contribution decisions of the type 3 voters. 76. The results were obtained much earlier than the publication date and presented at the 1977 Public Choice conference. 77. The intuition is twofold. All else equal, both candidates would like to locate near the center, because that’s where the median voter is. However, the disadvantaged candidate can win only by distancing himself or herself away from the advantaged candidate, which leads to an incentive to move away from the median. Mixing occurs because the advantaged candidate can win by matching any pure strategy of the disadvantaged candidate. 78. The instructions used neutral terminology rather than presenting the task as a voting decision. 79. Despite the problems with multiple equilibria, the experiments provide an interesting source of data for understanding coordination failure and the dynamics of behavior in coordination games. Later, we also discuss the QRE analysis of these games by Goeree and Holt (2005), which provides a possible explanation for the early-round differences in W and PR turnout rates and the eventual decline and convergence of the two turnout rates. 80. We chose to not to break ties randomly because there were already several random variables in the design (the assignment of voting costs and the assignment to parties), and this was simpler. Instead, ties paid the expected value of a random tie break. 81. When N = 3, the toss-up and landslide treatments are the same. 82. The upset rate equals the probability the minority candidate wins. 83. The close election rate is the probability the election is either tied or one away from a tie. That is, the probability a voter is pivotal. 84. The competition effect is also supported in a recent experiment by Grosser and Schram (2010). They compare turnout in twelve voter elections where the larger party can consist of six, seven, eight, or nine voters.

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85. The size effect is supported with the exception for the tossup races with twenty-seven versus fifty-one voters, where turnout was slightly more (less than half a percentage point) in the fifty-one-voter case than the twenty-seven-voter case. 86. The distribution of disturbances can be different from different individuals. See Rogers et al. (2009). With no restrictions on the distribution of disturbances, choice frequencies are not necessarily monotone and, in fact, can be anything. This is a general property of additive random utility models. See Haile, Hortascu, and Kosenok (2008) and Goeree, Holt, and Palfrey (2005). 87. The definition has been generalized to extensive form games (AQRE). Limit points of AQRE as λ → ∞ are sequential equilibria. 88. In order to pool all treatments together, the horizontal axis represents the normalized voting cost, that is, the difference between the voting cost and the equilibrium indifference point (which varies across treatments). 89. Their analysis can be extended to studying quasi-symmetric equilibria in asymmetric participation games. 90. Cason and Mui (2005) independently proposed QRE as an explanation to some results they observe in participation games. 91. Theoretically, there is a parallel between QRE in complete information turnout games with homogeneous costs and Bayesian equilibria of the turnout games with privately known costs because the privately known costs can be interpreted as additive payoff disturbances. 92. Some recent papers have cast doubt on the reliability of elicited beliefs from subjects during the course of a decision or game theory experiment. See Palfrey and Wang (2009) and several of the papers they cite. 93. Voters were assigned to parties in the following way. First, three voters were assigned to each party. Then the remaining six voters were each assigned to one or the other party by independent coin tosses. 94. There is a large and growing literature in political science that uses field experiments and natural experiments to study various informational effects on voter turnout. See, for example, Gerber and Green (2000) and Lassen (2005). 95. Early voters can vote in the second stage if they abstain in the first stage. 96. Surprisingly, turnout rates are 50% higher for early voters than late voters in the no-information treatment, contrary to the symmetric equilibrium turnout rates. This huge asymmetry suggests that the labeling of early voters and late voters may allow groups to coordinate on asymmetric turnout equilibria. 97. In the positive-information treatments, the game is a signaling game, which introduces additional possible equilibria and may even enable subjects to coordinate on asymmetric equilibria. They also conduct a “partners” treatment, with 99 repetitions, so the data may reflect a mixture of asymmetric equilibria. 98. Observed turnout in that treatment is slightly under 50%. 99. Purely instrumental voters would have an incentive to vote their true preference since there is no direct cost to voting, regardless of the (positive) probability their vote is decisive. 100. In some variations, only yes voters are required to make a contribution if the vote exceeds the quorum. 101. This is not equivalent to eliciting the beliefs about pivot probabilities. 102. The question of causality is more complicated. These two tasks (voting and reporting beliefs) are not entirely independent. By voting yes, a voter increase the probability that the quota is achieved. 103. That is, the calculus of voting involves conditioning on the event that a voter is pivotal. 104. Ladha, Miller, and Oppenheimer (unpublished working paper, 1999) also investigate strategic voting in information aggregation experiments. 105. The analysis assumes retrial is not possible. 106. Under unanimity, the outcome was A unless all voters voted for B. Under majority rule, the outcome was A unless a clear majority voted for B. 107. In six-person majority-rule juries, α signal voters voted for A only 79% of the time. However, sincere voting is a weak equilibrium with an even number of voters because the rules required a clear majority for A to win. As a result, in equilibrium α signal voters are actually indifferent between voting for A and B. 108. Specifically, the study found that majority rule leads to more false convictions than unanimity in large juries and that larger unanimous juries produce fewer false convictions than smaller unanimous juries. Nash equilibrium predicts the opposite effect in both cases. 109. In Guarnaschelli et al. (2000), a student monitor determined the state of the world by rolling a fair die, and subjects drew their own signals from a virtual urn on their computer screen. 110. See Ali and Kartik (2012) and Callander (2002) for information aggregation models of bandwagon effects in voting games. Equilibrium bandwagon effects can occur in these games in a way that mimics choice behavior in the herding equilibrium of Bikhchandani, Hirshleifer, and Welch (1992).

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Chapter 6 111. Communication is essentially unrestricted and implemented by a chat box on each subject’s computer screen. Messages can be either broadcast or targeted. 112. The exception is unanimity rule, which can achieve only a subset of the outcomes achievable by other voting rules. 113. The latter observation is a bit surprising, since the group efficient level of turnout coincides with the equilibrium level (100%) in the low-cost treatment. 114. All votes are sincere. A 0–0 tie after the first two stages is off the equilibrium path. 115. For example, in the low-cost treatment, the first voter abstains 33% of the time, and in the high-cost treatment, the third voter abstains more than 33% of the time following a 0–0 or 1–1 tie. 116. The expected effect of voting costs on both kinds of efficiency (higher costs lead to lower efficiency) were also observed. 117. Two of the π = 59 session had only only seven subjects, so there was not rematching of committees between elections in those sessions. 118. In some of their treatments, there is also an inefficient third equilibrium, where low-information voters mix. In addition, there can be asymmetric equilibria. Because the sessions are run using a “partners” repeated-game design for sixty repetitions and committees are very small (n = 3), it is plausible that different groups converge to different asymmetric equilibria. The authors don’t find evidence of these other kinds of equilibria in their data. 119. In the experiment, the uniformative signal was implemented as a statement on their computer screen that says, You are uninformed. 120. A few papers investigate more-general utility specifications in multiple dimensions, such as elliptical indifference curves, to allow for different intensities across issues. 121. There is a large literature on public goods mechanisms using side payments for producing efficient allocations, such as Groves mechanisms, the Groves-Ledyard mechanism, d’Aspremont and GérardVaret, and so forth. We are interested in problems where participants are endowed with voting rights. A few papers explore models that combine voting rights with side payments, and these are discussed in the section on vote markets. 122. The information structure in the standard storable votes model has incomplete information. In period t, voters know only their own valuation for the current issue but have only probabilistic information about other voters’ current and future valuations and their own future valuations. 123. The main variation is that voters always have one regular vote that they must use in each issue but are endowed at the beginning with B bonus votes, that they may cast in addition to their their regular votes. 124. Other methods, such as supermajority requirements, also give minorities more power. 125. This is similar to the voting scheme proposed by Casella and Gelman (2008). 126. Failure to reach agreement results is a random coin toss on every issue. 127. Observe that this mechanism is equivalent to a storable votes mechanism, where each voter is given twenty bonus votes but is allowed to use at most one bonus vote on any given issue. 128. In the binding-commitment case, voters were given physical ballots for each issue, and there was a trading period during which the ballots could exchange hands, in a manner similar to trading baseball cards. 129. In Casella, Llorente-Saguer, and Palfrey, no distributional information was given about the distribution of valuations. 130. Cadigan (2005) and Elbittar and Gomberg (2009). 131. Indeed, if anything the political science community is even more open minded about such behavioral relaxations of rational choice theory. Traditionally, the modal behavioral view in political science has been quite hostile to and suspicious of rational choice theory. See for example Green and Shapiro (1994).

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Grelak, Eric, and Koford Koford. 1997. A Re-Examination of the Fiorina-Plott and Eavey Voting Experiments: How Much Do Cardinal Payoffs Influence Outcomes? Journal of Economic Behavior and Organization 32(4): 571–89. Groseclose, Tim. 2001. A Model of Candidate Location When One Candidate Has a Valence Advantage. American Journal of Political Science 45: 862–86. Grosser, Jens, and Arthur Schram. 2006. Neighborhood Information Exchange and Voter Participation: An Experimental Study. American Political Science Review 100(2): 235–48. Grosser, Jens, and Arthur Schram. 2010. Public Opinion Polls, Voter Turnout, and Welfare: An Experimental Study. American Journal of Political Science 54(3): 700–17. Guarnaschelli, Serena, Richard D. McKelvey, and Thomas R. Palfrey. 2000. An Experimental Study of Jury Decision Rules. American Political Science Review 94(2): 407–23. Güth, Werner, and Erik van Damme. 1998. Information, Strategic Behavior, and Fairness in Ultimatum Bargaining: An Experimental Study. Journal of Mathematical Psychology 42: 227–47. Haile, P., A. Hortascu, and G. Kosenok. 2008. On the Empirical Content of Quantal Response Equilibrium. American Economic Review 91(1): 180–200. Herrera, Helios, Massimo Morelli, and Thomas R. Palfrey. 2014. Turnout and Power Sharing. Economic Journal 124(February): 131–62. Herzberg, Roberta, and Rick Wilson. 1988. Results on Sophisticated Voting in an Experimental Setting. Journal of Politics 50(May): 471–86 ———. 1991. Costly Agendas and Spatial Voting Games: Theory and Experiments on Agenda Access Costs. In T. Palfrey, ed., Contemporary Laboratory Research in Political Economy. Ann Arbor, MI: University of Michigan Press. Hortala-Vallve, Rafael, and Aniol Llorente-Saguer. 2010. A Simple Mechanism for Resolving Conflict. Games and Economic Behavior 70: 375–91. Hortala-Vallve, Rafael, Aniol Llorente-Saguer, and Rosemarie Nagel. 2013. The Role of Information in Different Bargaining Protocols. Experimental Economics 16(1): 88–113. Hsu, Li-Chen, C. C. Yang, and Chun-Lei Yang. 2008. Positive vs. Zero-Sum Majoritarian Ultimatum Games: An Experimental Study. Journal of Economic Behavior and Organization 68: 498–510. Hummel, Patrick. 2010. On the Nature of Equilibria in a Downsian Model with Candidate Valence. Games and Economic Behavior 70: 425–45. Hung, Angela, and Charles R. Plott. 2001. Information Cascades: Replication and an Extension to Majority Rule and Conformity-Rewarding Institutions. American Economic Review 91(5): 1508–20. Isaac, R. Mark, and Charles R. Plott. 1978. Cooperative Game Models of the Influence of the Closed Rule in Three Person, Majority Rule Committees: Theory and Experiment. In P. Ordeshook ed., Game Theory and Political Science. New York: New York University Press. Jackson, M., and H. Sonnenschein. 2007. Overcoming Incentive Constraints by Linking Decisions. Econometrica 75(1): 241–58. Jennings, C. Alan. 2004. Robert’s Rules for Dummies. Hoboken, NJ: Wiley. Kagel, J. H., and K. W. Wolfe. 2001. Tests of Fairness Models Based on Equity Considerations in a Three-Person Ultimatum Game. Experimental Economics 4: 203–19. Kalandrakis, T. 2004. A Three-Player Dynamic Majoritarian Bargaining Game. Journal of Economic Theory 16(2): 294–322. Kartal, M. 2013. Laboratory Elections with Endogenous Turnout: Proportional Representation versus Majoritarian Rule. Working paper, University of Vienna. Key, V. O. 1966. The Responsible Electorate. Cambridge, MA: Harvard University Press. Kinder, Donald, and Thomas R. Palfrey. 1993. Experimental Foundations of Political Science. Ann Arbor, MI: University of Michigan Press. Knez, M., and C. Camerer. 1995. Outside Options and Social Comparison in Three-player Ultimatum Game Experiments. Games and Economic Behavior 10: 165–94.

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Chapter 6 Kormendi, Roger, and Charles R. Plott. 1982. Committee Decisions under Alternative Procedural Rules. Journal of Economic Behavior and Organization 3: 175–95. Ladha, Krishna, Gary Miller, and Joseph Oppenheimer. 1999. Information Aggregation by Majority Rule: Theory and Experiments. Working paper. Washington University, St. Louis. Laing, James D., and Scott Olmsted. 1978. An Experimental and Game-Theoretic Study of Committees. In P. C. Ordeshook ed., Game Theory and Political Science. New York: New York University Press. Laing, James D., and Benjamin Slotznick. 1991. When Anyone Can Veto: A Laboratory Study of Committees Governed by Unanimous Rule. Behavioral Science 36(3): 179–95. Lassen, D. 2005. The Effect of Information on Voter Turnout: Evidence from a Natural Experiment. American Journal of Political Science 49(1): 103–18. Ledyard, John O. 1995. Public Goods Experiments. In J. Kagel and A. Roth, eds., Handbook of Experimental Economics, Vol. 1. Princeton, NJ: Princeton University Press. Levine, David, and Thomas R. Palfrey. 2007. The Pardox of Voter Participation. American Political Science Review 101(1): 143–58. Levine, Michael, and Charles Plott. 1977. Agenda Influence and Its Implications. Virginia Law Review 63: 561–604. Lupia, A. 1994. The Effect of Information on Voting Behavior and Electoral Outcomes: An Experimental Study of Direct Legislation. Public Choice 78(1): 65–86. McKelvey, Richard D. 1976. Intransitivities in Multidimensional Voting Models and Some Implications for Agenda Control. Journal of Economic Theory 12: 472–82. ———. 1979. General Conditions for Global Intransitivities in Formal Voting Models. Econometrica 47: 1085–1112. ———. 1991. An Experiment Test of a Stochastic Game Model of Committee Bargaining. In T. Palfrey, ed., Contemporary Laboratory Research in Political Economy. Ann Arbor, MI: University of Michigan Press. McKelvey, Richard D., and Richard Niemi. 1978. A Multistage Game Representation of Sophisticated Voting for Binary Procedures. Journal of Economic Theory 18: 1–22 McKelvey, Richard D., and Peter C. Ordeshook. 1978. Competitive Coalition Theory. In P. C. Ordeshook, ed., Competitive Coalition Theory. New York: New York University Press, 1–37. ———. 1979. An Experimental Test of Several Theories of Committee Decision-Making under Majority Rule. In S. J. Brams, A. Schotter, and G. Schwodiauer, eds., Applied Game Theory. Wurzburg: Physica Verlag. ———. 1980. Vote Trading: An Experimental Study. Public Choice 35(2): 151–84. ———. 1981. Experiments on the Core: Some Disconcerting Results for Majority Rule Voting Games. Journal of Conflict Resolution 25(December): 709–24. ———. 1982. Two-Candidate Elections without Majority Rule Equilibria: An Experimental Study. Simulation and Games 13(3): 311–35. ———. 1983. Some Experimental Results That Fail to Support the Competitive Solution. Public Choice 40(3): 281–91. ———. 1984a. An Experimental Study of the Effects of Procedural Rules on Committee Behavior. Journal of Politics 46(1): 182–205. ———. 1984b. Rational Expectations in Elections: Some Experimental Results Based on a Multidimensional Model. Public Choice 44: 61–102. ———. 1985a. Elections with Limited Information: A Fulfilled Expectations Model Using Contemporaneous Poll and Endorsement Data as Information Sources. Journal of Economic Theory 36: 55–85. ———. 1985b. Sequential Elections with Limited Information. American Journal of Political Science 29(3): 480–512. ———. 1990a. Information and Elections; Retrospective Voting and Rational Expectations, In J. Ferejohn and J. Kuklinski, eds., Information and Democratic Processes. UrbanaChampaign: University of Illinois Press, 281–312.

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———. 1990b. A Decade of Experimental Research on Spatial Models of Elections and Committees. In Melvin J. Hinich and James Enelow, eds., Government, Democracy, and Social Choice. Cambridge, UK: Cambridge University Press. McKelvey, Richard D., Peter C. Ordeshook, and Mark D. Winer. 1978. The Competitive Solution for N-Person Games Without Transferable Utility, with an Application to Committee Games. American Political Science Review 72(2): 599–615. McKelvey, Richard D., and R. Talbot Page. 2000. An Experimental Study of the Effects of Private Information in the Coase Theorem. Experimental Economics 3: 187–213. McKelvey, Richard D., and Thomas R. Palfrey. 1992. An Experimental Study of the Centipede Game. Econometrica 60: 803–36. ———. 1995. Quantal Response Equilibria for Normal Form Games. Games and Economic Behavior 10: 6–38. ———. 1998. Quantal Response Equilibria for Extensive Form Games. Experimental Economics 1: 9–41. Meirowitz, Adam. 2007. In Defense of Exclusionary Deliberation. Journal of Theoretical Politics 19: 301–28. Miller, Gary, Thomas Hammond, and Charles Kile. 1996. Bicameralism and the Core: An Experimental Study of Legislative Stability. Legislative Studies Quarterly 21(February): 83–103. Miller, Gary J., and Joe A. Oppenheimer. 1982. Universalism in Experimental Committees. American Political Science Review 76(3): 561–74. Morton, Rebecca. 2007. Why the Centipede Game is Important for Political Science. In John Aldrich, James Alt, and Arthur Lupia eds., Positive Changes in Political Science. Ann Arbor, MI: University of Michigan Press. Morton, Rebecca, and Thomas Rietz. 2008. Majority Requirements and Minority Representation. NYU Annual Survey of American Law 63: 691–725. Morton, Rebecca, and Jean-Robert Tyran. 2011. Let the Experts Decide? Asymmetric Information, Abstention and Coordination in Standing Committees. Games and Economic Behavior 72: 485–509. Morton, Rebecca, and Kenneth Williams. 1999. Information Asymmetries and Simultaneous versus Sequential Voting. American Political Science Review 93: 51–67. ———. 2001. Learning by Voting. Ann Arbor, MI: University of Michigan Press. Murnighan, J. Keith, J. W. Kim, and A. R. Metzger. 1993. The Volunteer Dilemma. Administrative Science Quarterly, 38: 515–38. Myerson, R, and M. Satterthwaite. 1983. Efficient Mechanisms for Bilateral Trading. Journal of Economic Theory 29: 265–81. Myerson, Roger, Thomas Rietz, and Robert Weber. 1998. Campaign Finance Levels as Coordinating Signals in Three-Way, Experimental Elections. Economics and Politics 10(3): 185–217. Myerson, Roger, and Robert Weber. 1993. A Theory of Voting Equilibria. American Political Science Review 87: 102–14. Nagel, R., and F.-F. Tang. 1998. Experimental Results on the Centipede Game in Normal Form: An Investigation of Learning. Journal of Mathematical Psychology 42: 356–84. Niskanan, William A., Jr. 1971. Bureaucracy and Representative Government. Chicago: AldineAtherton. Ochs, J. 1995. An Experimental Study of Games with Unique Mixed Strategy Equilibria. Games and Economic Behaviour 10: 202–17. Olson, M. 1965. The Logic of Collective Action. Cambridge, MA: Harvard University Press. Ordeshook, Peter C., and Thomas R. Palfrey. 1988. Agendas, Strategic Voting, and Signaling with Incomplete Information. American Journal of Political Science 32(2): 441–66. Ordeshook, Peter C., and Mark Winer. 1980. Coalitions and Spatial Policy Outcomes in Parliamentary Systems: Some Experimental Results. American Journal of Political Science 24(4): 730–52. Ostrom, E. 1990. Governing the Commons: The Evolution of Institutions for Collective Action. New York: Cambridge University Press.

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Chapter 6 Palfrey, Thomas R. 1989. A Mathematical Proof of Duverger’s Law. In Peter C. Ordeshook, ed., Models of Strategic Choice in Politics. Ann Arbor, MI: University of Michigan Press. ———. 2006. Laboratory Experiments. In Barry Weingast and Donald Wittman, eds., The Oxford Handbook of Political Economy. Oxford: Oxford University Press. ———. 2012. A Simple Common Value Auction. Working paper. California Institute of Technology. Palfrey, Thomas R., and Howard Rosenthal. 1983. A Strategic Calculus of Voting. Public Choice 41: 7–53. ———. 1984. Participation and the Provision of Discrete Public Goods: A Strategic Analysis. Journal of Public Economics 24: 171–93. ———. 1985. Voter Participation and Strategic Uncertainty. American Political Science Review. 79: 62–78. ———. 1988. Private Incentives in Social Dilemmas: The Effects of Incomplete Information and Altruism. Journal of Public Economics 35: 309–32. ———. 1991a. Testing Game-Theoretic Models of Free Riding: New Evidence on Probability Bias and Learning. In T. Palfrey, ed., Contemporary Laboratory Research in Political Economy. Ann Arbor, MI: University of Michigan Press. ———. 1991b. Testing for Effects of Cheap Talk in a Public Goods Game with Private Information. Games and Economic Behavior 3: 183–220. ———. 1994. Repeated Play, Cooperation, and Coordination: An Experimental Study. Review of Economic Studies 61: 545–65. Palfrey, Thomas, and Stephanie Wang. 2009. On Eliciting Beliefs in Strategic Games. Journal of Economic Behavior and Organization 71(2): 98–109. Plott, Charles R. 1967. A Notion of Equilibrium Under Majority Rule. American Economic Review 57: 787–806. ———. 1979. The Application of Laboratory Experimental Methods to the Public Choice. In C. S. Russell, eds., Collective Decision Making: Applications from Public Choice Theory. Baltimore: Johns Hopkins Press. 137–60. ———. 1991. A Comparative Analysis of Direct Democracy, Two-Candidate Elections and ThreeCandidate Elections in an Experimental Environment. In Thomas Palfrey, ed., Contemporary Laboratory Research in Political Economy. Ann Arbor, MI: University of Michigan Press. Plott, Charles R., and Michael E. Levine. 1978. A Model of Agenda Influence on Committee Decisions. American Economic Review 68(1): 146–60. Plott, Charles R., and Vernon L. Smith. 1978. An Expermiental Examination of Two Exchange Institutions. Review of Economic Studies 45: 133–53. Ponti, G., 2000. Cycles of Learning in the Centipede Game. Games and Economic Behavior 30: 115–41. Rapoport, Amnon, and Dan Felsenthal. 1990. Efficacy in Small Electorates with Plurality and Approval voting. Public Choice 64: 57–71. Rapoport, Amnon, Dan Felsenthal, and Zeev Moaz. 1988a. Tacit Cooperation in ThreeAlternative Noncooperative Voting Games: A New Model of Sophisticated Behavior Under the Plurality Procedure. Electoral Studies 7: 143–61. ———. 1988b. Proportional Representation: An Empirical Evaluation of Single-Stage NonRanked Voting Procedures. Public Choice 59: 151–65. ———. 1991. Sincere vs. Strategic Voting in Small Groups. In T. Palfrey. ed., Contemporary Laboratory Research in Political Economy. Ann Arbor, MI: University of Michigan Press. ———. 1993. Does it Really Make a Difference? An Empirical Evaluation of Five Voting Procedures. British Journal of Political Science 23: 1–27. Rietz, Thomas A. 1993. Implementing and Testing Risk Preference Induction Mechanisms in Experimental Sealed Bid Auctions. Journal of Risk and Uncertainty 7: 199–213. ———. 2008. Three-Way Experimental Election Results: Strategic Voting, Coordinated Outcomes and Duverger’s Law. In Charles Plott and Vernon Smith, eds., The Handbook of Experimental Economics Results. Amsterdam: Elsevier.

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Rietz, Thomas, Roger Myerson, and Robert Weber. 1998. Campaign Finance Levels as Coordinating Signals in Three-Way, Experimental Elections. Economics and Politics 10(3): 185–217. Riker, William H. 1971. An Experimental Examination of Formal and Informal Rules of a ThreePerson Game. In B. Lieberman, ed., Social Choice. New York: Gordon and Breach. Riker, William H., and S. Brams. 1973. The Paradox of Vote Trading. American Political Science Review 67: 1235–47. Riker, William H., and W. J. Zavoina. 1970. Rational Behavior in Politics: Evidence from a ThreePerson Game. American Political Science Review 64. Roberts, Henry M., III, Daniel H. Honemann, and Thomas Balch. 2011. Robert’s Rules of Order: Newly Revised (11th Edition). Cambridge, MD: Da Capo Press. Rogers, Brain, Thomas Palfrey, and Colin Camerer. 2009. Heterogeneous Quantal Response Equilibrium. Journal of Economic Theory 144(4): 1440–67. Romer, Thomas, and Howard Rosenthal. 1978. Political Resource Allocation, Controlled Agendas, and the Status Quo. Public Choice 33: 27–45. Roth, Alvin. 1995. Bargaining Experiments. In J. Kagel and A. Roth, eds., Handbook of Experimental Economics. Vol. 1. Princeton, NJ: Princeton University Press. Rubinstein, Ariel. 1982. Perfect Equilibrium in a Bargaining Model. Econometrica 50: 97–109. Salant, S. W., and E. Goodstein. 1990. Predicting Committee Behavior in Majority Rule Voting Experiments. Rand Journal of Economics 21(2): 293–313. Schofield, Norman. 1983. Generic Instability of Majority Rule. Review of Economic Studies 50: 695–705. Schofield, Norman, Bernard Grofman, and Scott L. Feld. 1988. The Core and the Stability of Group Choice in Spatial Voting Games. American Political Science Review 82(1): 195–211. Schram, Arthur, and Joep Sonnemans. 1996a. Voter Turnout as a Participation Game: An Experimental Investigation. International Journal of Game Theory 25: 385–406. ———. 1996b. Why People Vote: Experimental Evidence. Journal of Economic Psychology 17(4): 417–42. Schram, Arthur, and Frans van Winden. 1991. Why People Vote: Free Riding and the Production and Consumption of Social Pressure. Journal of Economic Psychology 12(4): 575–620. Shepsle, Kenneth, and Barry Weingast. 1981. Structure-Induced Equilibrium and Legislative Choice. Public Choice 37: 503–19 Smith, Vernon L. 1976. Experimental Economics: Induced Value Theory. American Economic Review 66: 274–79. Suleiman, Ramzi, David Budescu, and Amnon Rapoport. 2001. Provision of Step Level Public Goods with Uncertain Threshold and Continuous Contribution. Journal of Group Decision and Negotiation 10: 253–74. Sundali, J., A. Rapoport, and D. Seale. 1995. Coordination in Market Entry Games with Symmetric Players. Organizational Behavior and Human Decision Processes 64: 203–18. Tullock, G. 1971. The Charity of the Uncharitable. Economic Inquiry 9: 379–92. Tullock, G. 1980. Efficient Rent Seeking. In J. Buchanan, R. Tollison, G Tullock, eds., Toward a Theory of the Rent-Seeking Society. College Station, TX: Texas A&M University Press, 97–112. Tyran, J.-R. 2004. Voting When Money and Morals Conflict: An Experimental Test of Expressive Voting. Journal of Public Economics 88: 1645–64. van de Kragt, A., J. Orbell, and R. Dawes. 1983. The Minimal Contributing Set as a Solution to Public Goods Problems. American Political Science Review 77: 112–22. Wiseman, A., and C. Volden. 2007. Bargaining in Legislatures over Particularistic and Collective Goods. American Political Science Review 101(1): 79–92. ———. 2008. Bargaining in Legislatures over Particularistic and Collective Goods: Erratum. American Political Science Review 102(3): 385–86. Walker, James M., Roy Gardner, Andy Herr, and Elinor Ostrom. 2000. Collective Choice in the Commons: Experimental Results on Proposed Allocation Rules and Votes. Economic Journal 110: 212–34.

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Chapter 6 Walker, James M., V. Smith, and J. Cox. 1990. Inducing Risk Neutral Preferences: An Examination in a Controlled market Environment. Journal of Risk and Uncertainty 3: 5–24. Warwick, P. V., and J. N. Druckman. 2001. Portfolio Salience and the Proportionality of Payoffs in Coalition Government. British Journal of Political Science 31: 627–49. Weck-Hannemann, Hannelore. 1997. Do People Care About Democracy? An Experiment Exploring the Value of Voting Rights. Public Choice 91(1): 27–47 Williams, Kenneth C. 1991a. Advertising and Political Expenditures in a Spatial Election Game: An Experimental Investigation. Simulation and Games 22: 421–42. ———. 1991b. Candidate Convergence and Information Costs in Spatial Elections: An Experiment Analysis. In T. Palfrey, ed., Contemporary Laboratory Research in Political Economy. Ann Arbor, MI: University of Michigan Press. ———. 1994a. Sequential Elections with Retrospective Voting: Some Laboratory Experiments. Public Choice 80: 1–8. ———. 1994b. Spatial Elections with Endorsements and Uninformed Voters: Some Laboratory Experiments. Public Choice 80: 1–8. Wilson, Rick K. 1986a. Forward and Backward Agenda Procedures: Committee Experiments on Structurally Induced Equilibrium. Journal of Politics 48(2): 390–409. ———. 1986b. Results on the Condorcet Winner: A Committee Experiment on Time Constraints. Simulation and Games, 17217–43. ———. 2007. Voting and Agenda Setting in Political Science and Economics. In Jane Sell and Murray Webster, eds., Laboratory Experiments in the Social Sciences. Amsterdam: Elsevier. ———. 2008. Collective Choice Experiments. In Stephen Durlauf and Lawrence Blume, eds., The New Palgrave Dictionary of Economics. London: Palgrave Macmillan.

7 Experimental Economics across Subject Populations Guillaume R. Fréchette

I INTRODUCTION This review will cover results from experiments on different subject pools, none of which are the usual sample of undergraduate students: infrahumans (rats, pigeons, and monkeys), people living in a token economy (mostly mental institutions), children, the elderly, subjects that are representative of larger populations, and professionals.1 What can we learn from studying rats or patients with psychiatric issues? What is the interest in reviewing results from experiments on such different subjects? By analyzing experimental data from different subject pools, we can assess to what extent behavior across species or groups features similar patterns. There are similarities in behavior across humans despite many differences in background as well as between humans and other animals. Suppose, for instance, that one observed a puzzling behavior for the first time, say, something such as hyperbolic discounting, in an experiment with the standard subject pool of undergraduate college students. One reaction could be to think that this is an artifact of the method of discovery: either the subject pool, the size of the incentives, and so on. However, suppose a similar behavior was observed in rats, pigeons, children, patients suffering from depression, and the like. Then, it would seem to build a case, from the weight of evidence, that this is not simply an artifact of the standard economic experimental methods and subject pool, but rather a robust phenomenon. This, I think, is one of the crucial reasons for which experiments with nonstandard subject pools are interesting: they allow for a better test of the robustness of our theories and findings.2 The counterpart to the preceding point is that it also allows us to discover specific ways in which the behavior of these groups differs. This is also interesting in itself. Indeed, learning how specific groups differ from each other helps us gain a deeper understanding of the nature of the group itself. For example, studying children can shed light on questions such as nature versus nurture. For behaviors that are learned, it offers an opportunity to understand when they appear. Understanding how preferences are shaped by ageing may be key to designing optimal policies. Despite the ways in which these groups are interesting, two samples stand out as more obviously of interest to economists: the representative sample (i.e., representative of the

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population at large) and professionals (meaning people who work in an area of interest). Although most economic models typically do not specify who they apply to, the groups on which one would think it makes most sense to test, evaluate, or estimate economic models are a representative sample of the population or samples of specialists at a certain task. For example, the representative sample could be of particular interest for analyzing savings, labor-supply decisions, voting, and the like, while a sample of specialists could be used to study, for example, the behavior of professional traders in financial markets. In that sense, these two samples are the most natural to study. Yet these two samples do also present disadvantages, and, conversely, the other samples, which are somewhat more removed from our immediate interest, present advantages. There are four main disadvantages to studying representative samples and professionals. These are costs, availability, replicability, and the limits to control. Costs are usually an issue because the opportunity cost of participating in an experiment for a student is certainly lower than that of an average member of a large population or, even more, of a professional. For this reason, providing appropriate incentives when using these nonstandard samples can turn out to be particularly expensive, undermining the researcher’s ability to gather a sufficient amount of data. A second issue is availability. It is usually more difficult to have access to a representative sample or a pool of professionals, especially compared with how easy it is to recruit students. In fact, this explains why some of the research with professionals uses such unusual professionals: sports card traders, fruit pickers, tree planters, soccer players, and so on. These are not necessarily the typical professionals we have in mind, and their use often has more to do with the connections or personal interests of the authors, which make it easier for them to have access to these people. These first two factors, cost and availability, combine to form a much more important problem: the replicability of experiments with these samples is severely reduced. With a standard experiment, if one doubts the robustness of a particular result and thinks the result is caused by some of the details of the implementation, be it the instructions, the interface, or the specific parameters used. it is relatively easy to conduct an experiment that varies the aspects of concern. For topics that become popular, the tradition of repeating one’s control can by chance reveal important details. An example of this is Charness, Fréchette, and Kagel (2004), where the authors added in the player’s instructions a simple table to summarize the payoffs of the manager and employee in a gift exchange game. They found that this simple change substantially reduced the amount of gift exchange, suggesting that part of the previous results were simply due to misunderstanding the implications of the player’s actions. The limited replicability of experiments with representative samples and professionals is a nontrivial shortcoming. Finally, using representative samples or professionals often means having less control on the experimental environment. Subjects who are unaccustomed to written instructions and to abstractions can have a tendency to understand the environment with which they are presented differently from the way it is intended, introducing noise in the observed data. In particular, there is evidence of professionals behaving as if they are in their professional environment, even when this is not appropriate. Although this is instructive because it speaks to the importance of those aspects of their professional environment, it can be, at times, a nuisance. Experiments often test models or create environments that abstract from certain aspects of a situation. If the subjects cannot engage with this abstraction, it becomes difficult to understand their behavior.3

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Beside professionals and representative samples, the other nonstandard subject pools that I will review, namely, infrahumans, children, elderly, and token economies, are not immune from their own set of issues. In particular, the point about the limited replicability I made before applies to them as well. Maybe it applies less to animals, to the extent that most universities have animal labs; nonetheless, the ability to perform experiments with these groups seems much more limited than with the standard subject pool of undergraduate students. However, some of these samples allow for enhanced control and complete measurement, something that is difficult to achieve elsewhere. For example, in experiments with animals or in token economies, prices can be modified, not simply within the boundaries of a normal experimental period of a few hours, but for a sustained period of time: days, weeks, or even months. Similarly, changes in income can happen not only in the context of the experiment, as is the case for standard samples, but also with regard to the total disposable income for the period under study. Finally, all variables can be measured precisely, none of them requiring reliance on self-reports. Can we formalize how each of these groups is similar or different from the “agent” of our typical model, our subject of interest? Infrahumans have no market interactions, no (or probably very different) socialization, and a different neurological structure (even though they share some commonalities). Children have had no (or few) market interactions, some early socialization, and the same or possibly a different (still developing) neurological structure. Subjects in token economies have had market interactions, the same socialization, and the same or possibly different (malfunctioning) neurological structure. The elderly have had market interactions, the same socialization, and the same or possibly different (decaying) neurological structure. This provides a certain order of distance from the “ideal” subject going from furthest to closest and thus this serves as the organizing criterion to order the sections: infrahumans, children, token economies, elderly, and representative sample, professionals.4 Writing a review such as this one is challenging for a few reasons. For one thing, papers that have a subject pool in common may have nothing else that connects one to the other. Hence, going from one paper to the next is somewhat disconnected. I have not found a way around this except to try and group papers on related topics together when possible. However, in the discussion, I will come back to papers on a given topic across subject pools to tie everything together. The reader interested in a summary organized by choice task can skip directly to that section. Note, however, that many papers reviewed in the previous sections are not mentioned in the discussion because it considers only choice tasks that have been studied using multiple subject pools. Another difficulty is that, for some of these samples, the number of studies is too large to be covered in its entirety.5 The solution to this is imperfect and arbitrary, but it is the only one I could find. I will review only papers that came out in economic journal (or working papers that one could expect to come out in those journals). For samples that have fewer studies, such as infrahumans and token economies, I tried to be thorough; for the others, I focused on papers that are either significant in some way or on topics for which there are multiple papers. Because these samples are unusual, some papers are described in more detail than is typical in a review. In particular, procedures are described in some cases to help the reader better understand the results and how they relate to what is found with other samples. The structure of each section varies slightly, but in all of them I conclude with some observations about methodological issues that are particular to the group under discussion.6

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II INFRAHUMANS The history of economic experiments using infrahumans is about as old as the “rediscovery” of incentivized laboratory economic experiments with humans in the 1960s and 1970s.7 Almost all economic experiments with nonhuman animals that have been published in economic journals have been conducted by John Kagel and Raymond Battalio, who, over the years, have had a multitude of coauthors, the most frequent being Leonard Green, Don MacDonald, and Howard Rachlin. Their experiments used mostly rat and pigeon subjects, although some also used guinea pigs and cats. As many economists do not even know that there are papers reporting economic experiments conducted on animals, it might even be more puzzling to realize how well published they are. It is even more surprising when considering that the earlier papers were published at a time where laboratory experiments with humans were not common. For instance, of the four papers published in economic journals before 1985, four were in top journals: two were in the American Economic Review, one in the Journal of Political Economy, and one in the Quarterly Journal of Economics. One factor that probably contributed to this success may be difficult to appreciate now: support for the as-if model. The use of as-if (optimizing) models of behavior is now so deeply engrained in the training of economists that it is difficult to appreciate that this was not always the case. In fact, those familiar with work in political science know that rational choice is still debated as an approach in that field. Hence, at the time, showing that infrahumans displayed behavior consistent with the predictions of optimizing agents would have been appealing because it served to support the view that as-if models can be useful.8 At a more fundamental level, experiments with animals allow the researcher to perform manipulations that simply cannot be done with humans. For instance, the quantity of food available to an animal is its wealth/income. When an experimenter changes the quantity of food available to an animal, it is as if that animal’s income is changed. These changes can be important both in terms of the size of the income change and the duration of the change. Similar experimental interventions for humans seem problematic and even impossible. Hence, although animals present undeniable limitations, they also offer distinct advantages. In addition, understanding infrahuman behavior may help to shed light on naturenurture-type questions. If a behavior is observed both in infrahumans and young children but not in older children and adults, this would seem to suggest that such behavior is eliminated by socialization. Finally, it is interesting to note that this line of research has served as a conduit for economic ideas into other disciplines: psychology, biology, and neuroscience.9 Some aspects of experimental procedures that are common across those experiments are the following.10 The animals are offered choices through levers or keys between a number of options, namely, different kinds of foods and liquids (liquids or food pellets for rats and grains for pigeons), or different time delays to obtain rewards, or different lotteries over varying probabilities and reward amounts. Two basic designs are used: In closed-economy experiments, all food intake the animal receives is from within the experiment. In open-economy experiments, the food at stake within the experimental trials is in addition to some amount of food and water in their home cages. The amount of food and water outside of the experiment is sometimes unlimited, while in some other cases it is controlled to maintain the animal’s weight. The animal practices the task for a period, usually in forced-choice tasks (i.e., the animal is forced to try each lever); then

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there is a period where the animal explores, and at some point the animal’s behavior stabilizes (on average). A stability criterion is used to determine what part of the data will be analyzed and when to change treatments. Typically, the number of subjects is small (between two and eight subjects per treatment) and the number of decisions is large. Many such experiments use an ABA within-subject design (meaning first control, followed by treatment, and back to control), where the return to the original condition is used to verify that the behavior returns close to its original level in the first A block. The types of choice studied include: commodity choice, labor-supply behavior, choices over uncertain or risky outcomes, and intertemporal choices. Kagel and Battalio produced a sizeable body of work (more than 20 papers and a book (Kagel, Battalio, and Green 1995) about infrahuman experiments), with the first published paper appearing in 1975. In that paper (which includes multiple coauthors), they study consumption changes as a reaction to changes in the budget set to determine if those changes are consistent with Slutsky-Hicks demand functions (which we would now think of as testing the general axiom of revealed preferences, or GARP). In other words, after an income-compensated price change, does the consumption of the good with the lowered price increase? These questions over basic properties of choice (revealed preferences and the shape of demand functions) were the impetus for much of these coauthors’ early experiments. The design of their experiment, which involved rats as the subjects, is the following: There are a fixed number of lever presses per day (corresponding to the subjects’ income) to be allocated by the subject across the levers. Two levers, one for each of the two different food and/or liquid options, were available. Changing the total number of lever presses available changes what corresponds to income in a budget set. Either changing the quantity of good per lever press or the number of lever presses for each unit of good delivered, results in a change in the relative price of the two goods. The advantages of using rats for this study are that reporting and recording error of price and consumption are negligible.11 Income can be precisely controlled when price changes, while the commodities in question can be more or less substitutable (e.g., food or water or root beer and Tom Collins mix). Finally, environmental factors can be controlled. Treatments consisted of changes in the price of the goods while adjusting income to leave the original bundle just affordable. The data are consistent with Slutsky-Hicks demand functions—the animals consume more of the good that has fallen in price, resulting in downward-sloping income-compensated demand curves. Furthermore, the demand is quite responsive to price in the open-economy treatments where the commodities employed were inherently more substitutable (e.g., root beer vs. Tom Collins mix), while it responds very little to prices in the closed economy treatments where the goods were inherently less substitutable (e.g., food and water). This question was revisited using pigeons (Battalio, Green, and Kagel 1981), with which they verified the earlier results. That is, subjects consumed a previously unattainable bundle after an income-compensated price change. However, in a second series of studies that involved two price changes, subjects failed to adjust consumption enough to satisfy GARP. Figure 7.1 gives a representation of this. First, a subject faced budget 1 and consumed A. When the budget is changed to either 2 or 3, consumption adjusts to something like B or C , respectively. However, in the second wave of studies, the authors change the budget line to 2 first, and consumption moves to B, but they follow this by a move to budget line 3 and observe a movement in the expected direction, but not quite far enough to satisfy GARP, for example, C  . Although the authors do not

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Food payoffs B

C’

A C 2

1

3 Water payoffs

Figure 7.1: Testing GARP using income-compensated price changes.

determine exactly what causes this failure, the result is somewhat suggestive of some form of anchoring. Clearly, the preceding results imply downward-sloping, income-compensated demand curves, and this is explored in Kagel and others (1981). However, in this paper they go further and verify the simple law of demand, namely, that (noncompensated) demands are downward sloping, and they do this for both essential and nonessential commodities (food and water versus root beer and Tom Collins mix). Many of these results (and others that will be discussed in this section) were later confirmed in experiments with humans. Having established that basic principles of economic behavior applied to infrahumans, the investigators could sensibly proceed to use these subjects to look for a phenomenon that would be difficult to test for in humans— namely, the existence of Giffen goods. Giffen goods provide a stark theoretical example of the importance of distinguishing between income and substitution effects, but are they simply a theoretical construct, or can they be observed in practice? Using choices over quinine and root beer (rats prefer root beer to water and water to quinine), Battalio, Kagel, and Kogut (1991) showed the existence of upward-sloping demand for quinine in 50% (3 out of 6) of their subjects. Further, using straight income shifts, it was determined that quinine was strongly inferior for the rats with upward-sloping demand curves and was either weakly inferior or a normal good for those with downward-sloping demand. This confirmed that Giffen goods are not simply a theoretical curiosity and that their existence, in this case at least, follows from the factors the theory postulates. Beside choices over commodities, the authors also explored choices over consumption and leisure. This was accomplished by a simple change in procedures: now large numbers of lever presses, or key pecks, were required to gain access to a single commodity, with no restrictions on the amount of labor supplied. Originally presented in Battalio, Kagel, and Green (1979) but analyzed in more detail in Battalio and others (1981), these authors show that leisure is a normal good. These results are replicated in Battalio and Kagel (1985) using rats in experiments that excluded a variety of competing hypotheses to explain the animals’ behavior.12 The data on consumption and leisure trade-offs from pigeons and the data on choices over commodities from rats are analyzed together in Battalio, Dwyer, and Kagel (1987) to understand if such choice

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behavior in rats and pigeons can be reconciled with utility maximization as opposed to some other type(s) of behavior that mimic utility maximization. The approach is to first estimate demand functions and then to assess to what extent the estimated parameters correspond to the implications of various models. Specifically they consider six models. Three models are not utility-maximizing models: random “money” deciders and random goods deciders (see Becker, 1962); and the matching law, the dominant model of choice at that time with respect to animal behavior (Herrnstein, 1961). They also consider two models that can be conceptualized as utility-maximizing models: the minimum distance to a preferred point (quadratic utility functions) and the generalized minimum-needs hypothesis (constant elasticity of substitution demand functions). Finally, they test a sixth model, which they refer to as the representative consumer model that can be applied to either of the two utility-maximization models. The model that fares best is the minimum-needs hypothesis, indicating that their results are consistent with some form of utility maximization. However, the validity of standard aggregation methods for establishing a representative consumer model is soundly rejected. Another important group of papers tackles questions of decision making under uncertainty. It starts with Battalio, Kagel, and MacDonald (1985), which explores risk attitudes in rats and tests for transitivity over choices. They also investigate risk attitudes at varying levels of consumption, going from levels resulting in rapid weight loss to levels near satiation. Finally, they test for violations of the independence axiom of expected utility theory (EUT). Rats choose lotteries that give them different quantities of food with certain probabilities. The findings are that rats display risk aversion at all levels of consumption, including where consumption levels are insufficient to maintain weight. Finally, they observe violations of the independence axiom similar to those observed at the time in psychology experiments with humans using nonincentivized, description based choices. The exploration of the violations of the independence axiom is studied in greater detail in Kagel, MacDonald, and Battalio (1990), with the domain of study changed to focus on losses. The types of violations studied are Allais-type common ratio violations. That is, imagine subjects make two choices. First they choose between A and B and then between C and D: Choice 1 A: x2 with probability p x3 with probability 1 − p

B:

x1 with probability q x3 with probability 1 − q

Choice 2 C: x2 with probability rp x3 with probability 1 − p

D:

x1 with probability rq x3 with probability 1 − rq

In the table, p > q, x3 > x2 > x1 , and 0 < r < 1. A subject that chooses A over B (B over A) and then chooses D over C (C over D) violates EUT and, more specifically, the independence axiom. Some generalizations of EUT can accommodate such choices; in particular, the generalizations considered in that paper are the ones that generate indifference curves that fan out (they are not parallel lines in the Marschak-Machina triangle). To allow for losses, defined here as an outcome where less is better, the design is changed by using time delay to payoffs as the random variable. What they find is that although they can reproduce Allais-type violations (consistent with the fanningout hypothesis), in other areas of the unit probability triangle, they find fanning in,

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contrary to a leading explanation for common ratio effects at the time (Machina, 1987). They also show that similar results are obtained in experiments with human subjects. They followed up with further experiments documenting failures of EUT in MacDonald, Kagel, and Battalio (1991). In that paper they again confirm failure of the independence axiom and observe both fanning out and fanning in of indifference curves. Additionally, they directly test the betweeness axiom (a weakening of independence) and observe choices inconsistent with it. In particular, they observe not only fanning in and out, but also convex indifference curves. These and other results from the many experiments conducted by these authors are summarized in Economic Choice Theory by Kagel, Battalio, and Green (1995). One experiment that stands out, originally published in Kagel and Green (1987), studies time preferences in pigeons. They found preference reversals or dynamic inconsistencies. In particular, they observed a preference for immediate reward over a delayed larger reward, but if the options were both delayed, they observed a preference for the delayed larger reward. One interesting observation is that when these authors were writing, they believed this was one of their first observations of behavior where nonhuman animals might be different from humans. However, an important article has now established similar behavior in humans (Frederick, Loewenstein, and O’Donoghue 2002). To the best of my knowledge, after Battalio and Kagel’s last publication of an experiment with nonhuman subjects in 1991 (with Carl Kogut), 15 years passed before another experiment with infrahumans was published in an economics journal. In Chen, Lakshminarayanan, and Santos (2006), the authors report two series of experiments. In both of them, capuchin monkeys enter voluntarily in a chamber adjacent to their cage, where they can trade tokens for food. Each experiment has multiple sessions, and each session involves 12 trials. A monkey is not allowed more than 2 sessions per day. This is an open-economy design. In a trial, the monkey (who has a budget of tokens at its disposal) can trade a token with one of the two experimenters on each side of the chamber. Both experimenters present a cue (a certain number of pieces of food), the monkey gives one of the two experimenter a token, and that experimenter gives the monkey a certain number of pieces of food. In both treatments of experiment 1, the monkeys have a fixed budget and a choice of two fruits (presented to them before they make their choice). The second treatment differs from the control by changing the relative price of the two fruits and adjusting the budget to make the original bundle affordable. This experiment is similar to Kagel and others (1975) in that it allows testing if the monkeys adjust their consumption in the direction predicted by GARP. The experiment involved three monkeys. In experiment 2 there are three treatments. Each of them always involves only one fruit, but the two options vary the amount (deterministically or stochastically) as well as what is presented to the monkey before making its choice (either the amount to be received, less than the amount to be received, or more than the amount to be received). In the first treatment, one experimenter always presents and gives a single piece of food, while the other experimenter presents one piece of food but gives either one or two pieces (each with a 50% probability). In the second treatment, both experimenters provide a 50–50 gamble over one or two pieces of fruit, but they differ in whether they initially display one or two pieces of fruit, framing the marginal piece of fruit as a gain or loss. In the third treatment, both experimenters give one piece of fruit with certainty but differ only in whether they initially displayed one or two pieces of fruit. The experiment involved 5 monkeys.

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The results from the first experiment establish that, as in Kagel and others (1975), the monkeys’ behavior is consistent with GARP. It also serves to show that their (novel) procedures, when applied to new and unexplored issues, were not likely to be responsible for the behavior reported. Note, however, that Kagel and others had more price changes, making it more difficult for the behavior to be consistent with GARP. The results from the first treatment of the second experiment are that monkeys prefer the option that stochastically dominates the other (in 87% of trials). This is similar to results from earlier experiments on rats using procedures with forced-choice trials.13 The second treatment (where both choices result in the same lottery) reveals that the monkeys prefer the option which presents one rather than two pieces of food (in 71% of the trials). Hence their choices exhibit reference dependence in that they prefer the frame in which they make gains rather than losses. The third treatment finds that 79% of choices are in favor of the option that displays a single piece of fruit (in this case both options yield the same certain reward of one piece). Hence, treatments 2 and 3 taken together show that the option that presents only one piece of fruit increases in popularity by eight percentage points when going from a situation where the outcome is a lottery (over one or two pieces of fruits) to a situation where monkeys receive only one piece of fruit. From this they conclude “this effect [reference dependence] is not confined to risky choices and, when combined with experiment 2, suggests that capuchins are not just reference-dependent but loss-averse,” since losses loom larger than gains in both cases. The first and last papers summarized in this section (Kagel et al. 1975; Chen, Lakshminarayanan, and Santos 2006) illustrate two extremes with respect to economic theory. The first experiment established that animal behavior was in line with basic economic principles. The second one suggests the presence in animals of biases that have been documented in humans and that violate basic expected utility theory. This is also consistent with much of the research conducted by Battalio and Kagel. That is to say, experiments on static models of choice between commodities and labor-supply behavior tend to find support for the predictions of standard economic theory. However, when moving to choices over uncertain or risky outcomes and when choosing over timedated goods, animals exhibit biases similar to those of humans, whether it be Allais-type violations, changes over risk preferences between the win and loss domains, or temporal inconsistency in choices. Finally, results indicating context-dependent choices in the spirit of some of the Chen and others’ results have been observed in other species, for instance, bees, gray jays (Shafir, Waite, and Smith 2002), and hummingbirds (Bateson, Healy, and Hurley 2003). II.A Methodological Notes By the very nature of the subject pool, experiments with infrahumans must let the subjects learn about their options through experimentation. On the other hand, most experiments published in economic journals describe the options to subjects such that a subject could theoretically determine what he or she wants to do without any experience. Some psychologists, however, use methods similar to those used on nonhumans with humans. As discussed in detail in Erev and Haruvy (Chapter 10), experiments using the paradigm of decisions from experience often lead to different results than those based on the paradigm of decisions from description, even for some very well-established phenomena. More specifically, contrary to the evidence from the research on prospect theory that subjects overweight events with small probabilities, when using a decision

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from experience paradigm, subjects underweight the probability of rare events. The relevance of this finding for experimental research on infrahumans is evident. When a difference in behavior between infrahumans and humans is observed, care must be taken when attributing the source of the difference to either socialization or cognitive ability. In some cases, the source of the divergence could simply be the different experimental methodologies.

III CHILDREN Experiments on children have a long history in psychology, dating back at least to early in the last century. In economics, however, their history is much more recent, with the first published paper reporting an experiment with children as subjects appearing in 2000.14 Much of the early research using children in economics has been conducted by William Harbaugh, Kate Krause, and varying coauthors, although others have contributed to this literature. Just like with nonhuman animals, if a behavior is observed in young children as well as in adults (the regular subject pool), then it is suggestive of a more robust and universal phenomena, as young children have had much less exposure to culture and to market institutions. Similarly, if a behavior is observed in young children but not in older children and adults, then it suggests a learned behavior. Understanding when and how humans learn is of interest in itself. However, it also is noteworthy because such behavior is less likely to be universal, as it is mediated by the specific culture and education of the group being studied. Suppose, for instance, that experiments conducted in the United States with the standard subject pool observe a certain behavior, and experiments with American children reveal that this behavior is not present in children of a certain age. This would suggest that similar experiments with the standard subject pool of different countries with different cultures may be worth pursuing. Also of interest is the fact that children have little to no market experience. Using variation across children in how much market interactions they have (some children enter the labor market early by babysitting; others have a weekly allowance to spend as they wish) may help to understand the role of market institutions in mediating economic behaviors. Finally, studying children and their parents can help understand the extent of and the process of cultural transmission. Relatedly, it allows us to explore questions such as the following: Where do preferences come from? (Think about risk or time preference, for instance.) Are they learned from our parents, and thus malleable, or are some of them transmitted genetically? Is there an age at which these preferences stop changing? Answers to these questions matter for public policy. Harbaugh and Krausse (2000) study altruism using a typical linear public good game, also known as a voluntary contribution mechanism (VCM) game. Subjects are allocated tokens that they can keep for themselves or invest in a public account that has a known return for all members of the group (the return to the donor of this investment is known as the marginal per capita return, or MPCR).15 Parameters are such that everyone investing everything in the public account is efficient, but keeping tokens in the private account is individually rational. In their study, group size is 6 and the number of repetitions is either fixed at 10 or random (between 4 and 8). They have treatments with a MPCR of 0.50 and 0.33. Participants are first- through seventh-grade students. The experiments are conducted with poker chips that can be exchanged for goods (fancy

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pencils, small stuffed animals, super balls, etc.) at the end of the experiment. Subjects are given 5 tokens before each round, and the exchange rate corresponds to approximately 10¢ per token. The results indicate that initial contributions are positive and that they react positively to the MPCR. Furthermore, students who have spent a longer fraction of their life at the school where the study was conducted contributed more. Many other factors considered by the authors were found to have no statistically significant effect: age, gender, number of siblings, single-parent household, allowance, TV watching, or church attendance. Unlike in VCM games with the standard college-age population, contributions increase slightly over time, except for children 11.5 years and older, for whom iterations decrease contributions, as with college age students. Peters and others (2004) also study the VCM game. Their main interest is to test the notion that if parents are altruistic, then it might be in the self-interest of children to maximize family income even if they are not altruists themselves (Becker’s Rotten Kid Theorem). In a VCM game, this would predict that children would contribute to the public good when playing with their family (but not with strangers) because they expect returns later on. The adults’ range in age between 34 and 50 (average 42), while the children are between 9 and 16 (average 11). The game is repeated 24 periods in blocks of 8 periods, where participants play first with strangers, then with their family, and then strangers again or family, strangers, family. Families vary in size (3 or 4 members) and composition. Some key findings are that (1) children give more to family members than to strangers; (2) parents give more to family members than to strangers; (3) parents give more than children in both conditions; and (4) contributions tend to decrease over time in every condition. To better understand the reasons why parents give to both their children and other children, they conducted an additional (strangers) treatment in which parents are grouped with other parents with whom they would not be familiar. There is no statistical difference between contributions in the family condition and the strangers’ condition (where they play with other parents). Note, however, that the authors compare all periods and do not report comparisons for the last periods. Looking at their figures, the drop in contributions is more pronounced for strangers than families, and thus they may be different by the end. Taking the data of both studies together suggests that the standard result from VCM experiments, which is that contributions decrease over repetitions, might appear only in the early teens. Peters and others (2004) do not find an effect of age on contributions, but their children are older than those used by Harbaugh and Krausse (2000). Other results are in line with findings using undergraduate students: contribution levels react positively to the MPCR. Both studies also suggest that close attachment to a group (either a family or a school in which one has received most of their education) leads to higher contributions. Other papers have investigated other-regarding preferences in children. Harbaugh, Krausse, Liday, and Vesterlund (2002) study trust games (also known as investment games). The general structure of a trust game is the following: The A player has some tokens, dollars, or other quantity to start with. He or she has a choice to send something to player B. What is sent is multiplied by a known factor. The B player can then send something back to player A. The final payoff for player A is equal to what he or she kept, plus what he or she received from player B. The payoff for player B is equal to what he or she kept. Player A is sometimes referred to as the truster and player B, the trustee (or first and second sender, respectively). The specific version of that game implemented in this project gave four tokens to player A, and what was passed to player B was multiplied by three. They used the strategy method, meaning that B players indicated what they

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would do for any of the five possible amounts A might send them. They used children from third, sixth, ninth, and twelfth grades. They asked the A player to make multiple transfers, one to a child of each grade and one to an adult. The adult’s decisions were mimicked by averaging the decisions of subjects in previous experiments. B players were asked for their returns separately for each possible grade of player A. For third graders, each token was worth approximately 25¢ at a portable toy store brought to school. Other grades were paid 25¢ per token. The findings indicate very little variations in what A players send to B as a function of B’s grade (age). On average 1.32 tokens (out of the 4) are passed. The amount A players send decreases as their score on a survey measure of trust increases (and thus suggests that this survey measure may be misleading), the birth order of the child has a positive impact, and the relative height of the child also increases the amount sent. Note that the age is found to have no effect. As for B players, the main factor affecting what they return is what they were sent. Nothing else beside the A player’s grade has an impact, and that is a small positive one. For example, the predicted difference between what is sent back to a third grader and a sixth grader is only one-tenth of a token. Other-regarding preferences are investigated through individual decisions about allocations of payoffs to a group in Sutter and others (2010). Using Austrian children in grades 3, 5, 7, 9, and 11, the experiment consists of selecting 1 of 3 distributions of payoffs for a group of 3 players. Subjects are matched in groups of 3, with randomly assigned positions one, two, and three; with the preference of position 2 implemented (thus 2 receives the middle income). This is done 8 times, each time with a different set of options. The authors use those choices to categorize subjects according to certain types of other regarding preferences. Incentives were varied for younger and older kids but were all monetary. The findings are that some choices do not vary with age while others do. These patterns are different for boys and girls. More specifically, choices that the authors categorize as corresponding to selfish preferences and ERC type preferences (Bolton and Ockenfels 2000) are similar for both genders. While choices corresponding to Fehr and Schmidt– (1999) type preferences are decreasing with age for both genders. When it comes to efficiency, it is fairly constant across ages for girls while it increases for boys and maximin-type preferences increase with age for girls, while it is mostly constant for boys. One caveat is that preferences are not uniquely identified in all choices. In particular, selfishness is uniquely identified in only two choices, while efficiency is uniquely identified in all choices. This can lead to problems. For instance, imagine that subjects prefer efficiency at all ages but sometimes make mistakes. However, they make fewer mistakes as they become older. Then it is possible for this to result in a decreasing fraction of subjects characterized as selfish and an increasing fraction of efficiency types, when, in fact, preferences are stable. Another area of research with ties to questions about other-regarding preferences is bargaining. Harbaugh, Krause, and Liday (2003) study the behavior of children in second, fourth, fifth, ninth, and twelfth grades in a dictator game and an ultimatum game.16 In the ultimatum game, a proposer has control of a sum of money; he or she offers a division of that money to a responder, who can accept (in which case they each get their part of the proposed division) or reject (in which case they both get nothing). The dictator game is similar but eliminates the possibility for the second mover to accept or reject (the dictator game is an individual-decision problem). For both games, subjects played in both roles (something that is not standard in adult experiments). They had 10 tokens to play with (per game), these tokens were exchanged for goods at a rate of about 25¢ (per token) for the youngest children, they were exchanged for

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money (25¢ ) for the ninth graders and 50¢ for the twelfth graders. They find that the tokens offered increase substantially in both the dictator game and the ultimatum game going from grade 2 to grade 4. This increase is fourfold in the dictator game, going from 3.5% to 14% of the endowment, while for the ultimatum game it goes from 35% to 41%. Rejection rates are relatively constant at about 10%, despite the differences in offers. Hence, younger children accept lower offers than older children. At all ages, average offers are substantially higher in the ultimatum game than in the dictator game, indicating that even young children react to the strategic nature of the games.17 Harbaugh, Krause, and Vesterlund (2001) study choices in 7- and 11-year-old children and college undergraduates to see to what extent they respect GARP. The subjects had to select from 11 different choice sets. Each choice set consisted of a finite number of alternatives (between 3 and 7 bundles). The goods were small bags of chips and boxes of fruit juice. Once all the choices were made, one of the 11 choices was randomly selected to be consumed. The subjects were shown all 11 choices 3 times and they had the opportunity to change their choice each time. The results indicate that some violations are present at all ages but much less than if choices were random, with these violations decreasing with age. Random choices would yield 81% of violations, whereas second graders have 39% of violations, sixth graders exhibit 19% of violations, and undergrads have 18% of violations. However, the severity of violations as measured by Afriat’s index does not change much with age.18 Random choices in this study would result in an Afriat index of 0.65. What they found is an index of 0.93 for second graders, 0.96 for sixth graders, and 0.94 for undergraduates, and these numbers are not statistically different. List and Millimet (2008) use a task similar to Harbaugh, Krause, and Vesterlund (2001); they also have 11 choices over chips and boxes of juice to explore the impact of market activity on GARP violations.19 Their experiments were conducted at malls that also host sports card shows. There they recruited youths ages 6 to 17 (on average about 11) to participate in their experiment. They divided them in three groups: two treatments, one where the experiment ended after the GARP task and one where subjects were given a gift of sports cards they could trade at the show after doing the GARP task. Subjects who had never previously attended a sports card show were randomly assigned to these two treatments. The third group consisted of subjects who had prior experience at sports card shows (they were placed in the no gift treatment). Seven months later, these subjects were invited back to do the GARP task again: the two different dates are referred to as round 1 and round 2. Attrition between the two dates was important, with only 420 subjects of the original 819 coming back in round 2. They report that in round 1, subjects who had not previously been to sports card shows displayed about 4 violations (out of 11), whereas subjects who had been to such shows displayed only about 2 mistakes. Seven months later, the violations fell in all groups (an average reduction of between 0.3 to 1.0 choices), but they fell the most among subjects assigned to the gift treatment who then decided to participate in the sports card show. The authors use econometric methods to tackle the various challenges of this kind of data (for instance, the mass of subjects with no violation) and to control for confounding factors. Taking the data at face value, they find that market experience decreases GARP violations. However, once they control for endogeneity, the effect disappears. On the other hand, age is found to have an impact in most specifications (older children make fewer mistakes). More specifically, distinguishing the effect of market experience among these treatments is not easy as there are multiple levels of endogeneity: who was already going to

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sports card shows is not exogenous; when assigned to the no-gift treatment, afterward actually not attending the show is not exogenous; when assigned to the gift treatment, afterward actually attending the show is not exogenous; and coming back for round 2 of the experiment is not exogenous. Hence, the paper reports multiple regressions, some performed on a subset that excludes subjects with prior experience. In addition, some specifications exclude the subjects whose behavior after the experiment did not correspond to the desired treatment (i.e., subjects in the gift treatment who did not go to the show or subjects in the no-gift treatment who did). Note that this does not eliminate endogeneity, but it does reduce the problem. They also perform an estimation, where they preserve these subjects but instrument for going to the show once in the experiment. Going from the full sample to the restricted sample reduces the magnitude of the effect of market experience by half (from about 1 to around 0.4—that is 0.4 fewer mistakes out of 11 choices). Once they instrument for participation at the show, the estimate drops to 0.15 fewer mistakes out of 11 choices, but the effect is no longer significant. Note, on the other hand, that the effect of age is significant (in all but one specification) and the magnitude of its impact is always at about 0.5 for the full or restricted sample, with or without IV (this means 0.5 fewer mistakes per year). Some of the results of List and Millimet (2008) do not line up with those of Harbaugh, Krause, and Berry (2001). In particular, Harbaugh and others report, on average, 4.3 violations (out of 11) for 7 years old and 2.1 violations for 11 years old. The List and Millimet subjects, who are on average 11, make about 4 mistakes, and the ones who have prior experience at sports card shows make 1.9 mistakes. In other words, the behavior of the 11 year olds of Harbaugh and others is similar to subjects with market experience in List and Millimet. Similarly, the youngest subjects in Harbaugh and others behave much like older subjects in List and Millimet. These differences could be due to differences in procedures or subject pools. Together, however, they both support the view that GARP violations decrease with age (at least between 7 and 11). The evidence with respect to the impact of market experience is less clear. In another paper, Harbaugh, Krausse, and Vesterlund (2001) investigate the presence of the endowment effect in children attending kindergarten, third grade, and fifth grade, as well as among undergraduates. Subjects are given one good (the endowment) and then an offer to trade it for a different one. The choice is repeated for 4 pairs of goods (3 in the case of undergraduates). The authors measure the endowment effect as the difference between the probability that the subject will choose good A when he or she is endowed with good A versus the probability that he or she will choose A when endowed with a different good. The endowment boost is defined as the average, between the two goods, of the probability that a subject chose a good when they were endowed with it as opposed to when they were not. The average endowment boost across pairs of goods is 3.1 for kindergartners, 1.5 for third graders, 3.9 for fifth graders, and 3.5 for undergraduates. But there are no statistical differences in the endowment boost across ages. Finally, Bettinger and Slonim (2007) study intertemporal choices among children ages 5 to 16. They also relate the children’s behavior to information about their parents. The children are offered compensation (in the form of Toys-R-Us gift certificates) at two sets of dates: the first set being immediately or 2 months in the future and the second set being 2 months or 4 months later. A key result is that more children are consistent with hyperbolic discounting than not. They also find that patience increases with age, and boys are less patient than girls. About a quarter of children make choices inconsistent with any rational model of choice, and this fraction decreases with age. Finally, family

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income, the parent’s education, or the parent’s patience (measured as for the children but using money) do not significantly correlate with the children’s patience. III.A Methodological Notes Two issues that arise with children are (1) how to incentivize them and (2) how to explain the task. With respect to incentivizing, for children of a certain age, money is appropriate, and many of the studies with children simply use money, but for younger children, such as kindergartners, it may not be ideal. The approach used by Harbaugh, Krause and coauthors is to pay children with tokens that can be used to buy toys in a movable store they bring with them and show to the kids before doing the experiment. Explaining procedures to children forces the investigators to be extremely clear, which is always good practice. However, the need for clarity and simplicity sometimes makes it impossible (or at least impractical) to use certain methods, such as the BeckerDeGroot-Marschak (BDM) mechanism (Becker, DeGroot, and Marschak 1964) to elicit valuations. Hence, just as with animal experiments, certain comparisons across the standard subjects and children are confounded with methodological differences. To the extent that results show similarities across the samples, this may not be an important concern, but in cases of differences, it is certainly worth thinking about.

IV TOKEN ECONOMIES Token economies were developed by psychologists as a mechanism for modifying the behavior of institutionalized individuals. They are mostly closed systems in the sense that individuals who are part of token economies spend the majority of their time in that environment and their earnings and consumption also occur, for the most part, in the system. Typically, individuals in token economies earn tokens for work such as making beds, cleaning bathrooms, and simple factory jobs. They can spend their earnings on food, cigarettes, movies, clothing, and the like. However, as will be seen shortly, token economies are not limited to institutionalized individuals. Experiments in token economies that address economic questions started with Ayllon and Azrin (1965). They changed the relative wage of different tasks to determine if wages can be used to induce individuals to change to their less-preferred work. They found that, indeed, they could influence job selection. More studies followed in psychology (see Tarr 1976). The first mention of token economies in an economics journal is in a communication published in 1972 in the Journal of Political Economy authored by John Kagel. He makes an argument for why token economies might be useful in testing economic theories. John Kagel and Raymond Battalio were students of Robert Basmann, an econometrician at Purdue at the time. Basmann wanted data to be more closely connected to the primitives of the models. For instance, having choices of multiple subjects over time allowed tests of GARP without making the strong aggregation assumptions that are necessary if one has only cross-sectional data. This desire for data that corresponded to the primitives of the model led Kagel and Battalio first to token economies, effectively very early field experiments, and then, via their psychologist collaborators, to infrahuman experiments. Panel data are now much more common, and some of the advantages that led Kagel and Battalio to use token economies are more easily available nowadays using the

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standard subject pool of undergraduate students. Nonetheless, token economies present a few advantages over the standard subject pool. The most important one is that, unlike in a standard experiment, the entire economic ecosystem is observed. In a standard experiment, much of the income and consumption of subjects happens outside of the laboratory. The same is not true in a token economy, and thus a token economy provides more control. On the other hand, this control is limited, as it cannot interfere with the primary purpose of the token economy, which is to reinforce “good” behavior. A token economy also provides precise measurement of variables of interest. Although this is in part true of standard experiments, it is not always so. In particular, behavior that may depend on total income (not simply experimental income) can rely only on reported income in a standard experiment. In a token economy, the tokens one owns are his or her income. The first actual study using data from a token economy to appear in an economics journal was Battalio and others (1973). They used data from the female ward for chronic psychotics at the Central Islip State Hospital in New York. The experimental variation was to change the relative prices for bundles of goods. That is, each good was placed in one of three groups, and the prices of goods in that group were sometimes doubled and sometimes halved. The sequence of changes followed the standard ABA design. The experiment took place over a period of 7 weeks and relative prices were the same for 1 to 2 weeks (although this was not known to the subjects). Patients were also unaware that they were taking part in an experiment. The experiment focused on whether individual consumption patterns are consistent with revealed preference theory (GARP). Furthermore, they highlighted the role of recording mistakes in limiting the ability to test GARP. They showed that even small reporting errors can lead to the incorrect rejection of the model. In their data, they have two independent measurements of consumption (the records taken at the time of sale, and the total tokens spent per patient in a week—tokens had the patient’s name stamped on them), and thus they can evaluate the extent of measurement error (which varied on average by 3.6%; Battalio, Kagel, and Reynolds 1977). Although they use the sales record for the first test, in case of a rejection, they then look for any possible mismeasurement consistent with the week’s total that would render the observations consistent with GARP. Only when both tests fail do they consider the data to reject the theory. What they find is that for 19 of the 38 subjects, the data satisfy GARP for all weeks. For most of the remaining 19 subjects, the contradiction occurs in a single pair of weeks. In fact, for 17 of these 19 subjects, there exists an allocation of the token difference between the two measures such that the data from all weeks is consistent with the model. Hence, behavior of only 2 out of the 38 subjects clearly rejects the model. Battalio, Kagel, and coauthors studied the Islip patients in multiple additional papers (Battalio et al. 1974; Basmann, Battalio, and Kagel 1976; Kagel et al. 1977) and their data were revisited in Cox (1997). These papers also investigated varying aspects of demand behavior, except for Kagel and others, which focused on labor-supply decisions. Another token economy studied consisted of three groups of volunteer subjects in an experiment on the impact of cannabis consumption on productivity. The subjects were paid to produce woolen belts on small portable hand looms at the Addiction Research Foundation in Ontario, Canada, with cannabis freely available, along with required smoking at a fixed time each day.20 This cannabis economy was studied on its own in two papers: Battalio, Kagel, and Reynolds (1978) studying the distribution of earnings and Kagel, Battalio, and Miles (1980), which examines the impact of marijuana consumption on productivity.

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The Islip data were also used in conjunction with the cannabis economy data in Battalio, Kagel, and Reynolds (1977). In that paper, they use these two token economies to determine if, in an economy where the sole sources of variation in earnings are due to variations in ability and effort, the earnings are more compressed than with typical field data. That is, a host of factors could account for differences in labor income in field settings such as chance, differences in cost of training across occupations, differences due to market failures such as inability to borrow the funds to finance training, and others. Some contend that ability and work-leisure trade-offs do not vary enough across individuals to explain the extent of variations observed in income. In the token economies, the work is simple enough that no training is necessary; everyone can work if they want to, and they can work as much as they want. Hence, the sole sources of variation in earnings in those token economies are ability and leisure decisions. What they show is that there are important variations in income in both cases. For instance, in both the Islip (25 subjects over 5 weeks) and cannabis (56 subjects over 3 months) economies, the maximum income is 10 times as large as the lowest. However, there is slightly more compression in the Cannabis economy, where the age distribution and subject characteristics were much more compressed.21 In fact, the Gini coefficients for both token economies fall within the range of multiple estimates from the United States, India, and the United Kingdom. Other summary statistics also confirm that variations in the token economies are similar to variations in earnings in the United States. Although this by no means proves that ability and work-leisure trade-offs explain the variation in earnings at the national level, it does show that those two factors by themselves can generate such variation and that in an environment without nepotism, discrimination, or other barriers to being able to work, earnings can vary greatly across individuals. The two papers described are illustrative of the work that has been performed using token economies, namely, that economic behavior in those environments is consistent with evidence obtained elsewhere and with the predictions of economic theory. For instance Varian (2006), in his review of the history of revealed preferences studies, reports that the evidence from these experiments is consistent with aggregate time-series data. The experimental work with token economies also manages to venture in areas that cannot be tackled with the standard subject pool such as the distribution of income. IV.A Methodological Notes Although token economies provide an ongoing economic system to study with much precision and completeness (it is one of the rare occurrence of data with humans where prices can be manipulated and both consumption and income are known), they also impose technical limitations. In particular, many experimental variations of potential interest would be unacceptable. Token economies have largely gone out of fashion in psychology, and an experiment like the cannabis economy is quite expensive and time consuming, so it would be hard to get a grant these days to study strictly economic issues in such a setting.

V ELDERLY With the population of developed countries aging and older individuals controlling a substantial amount of wealth, the importance of research on the elderly can only grow. This group, however, does not present many advantages as a group to study. It is not convenient (one needs to take the laboratory to them), interacting via computers is

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still difficult for many elderly, and for some of them, abstract instructions (and even written instructions) can be difficult to follow. One advantage of studying this group is that it allows us to gain an understanding of specific brain functions on behavior, since aging does not affect all brain functions equally. However, as I pointed out for the other groups: if a behavior is observed in the standard subject pool and in the elderly, this is further evidence of a robust phenomenon. The earliest laboratory study of older adults that I could identify in economics is a 2005 publication by Kovalchik and others (2005). They study two groups, 51 college students aged between 18 and 26 and 50 elderly aged between 70 and 95. The elderly subjects were neurologically healthy (they served as a control group for Alzheimer research). The experiment addresses four areas: overconfidence, risk preference, the endowment effect, and strategic thinking. More specifically, in the first task subjects answer 20 trivia questions, after which they are asked their assessment of the percentage they got right (50, 60, 70, . . . , 100). This is followed by two gambling tasks, in which subjects pick a fixed number of cards from either of two decks, decks A and B. In the first task, they pick 50 cards, while in the second task, they pick six cards. One deck has a negative average payoff (deck A), while the other has a positive average payoff (deck B), and the deck with the positive average payoff has a smaller variance. In the first case, subjects know nothing about the two decks in advance. Hence, there is no optimal strategy, but in neuroscience, a choice of A is seen as a mistake, as they think subjects should learn to pick B. In the second case, subjects are shown the 10 cards in both decks before the cards are shuffled. In a third task, the investigators assign each subject to be either a buyer or seller, and then they elicit the willingness to pay or willingness to accept payment for a mug. To finish, they play a beauty contest game in groups of 9. They select a number between 0 and 100. The subject that states the number closest to two-thirds of the average of the 9 numbers wins $20. Overall, the results indicate more similarities than differences as a function of age: 1. In the beauty contest, both groups show a first cluster of data around 33 and a second cluster around 22. 2. With respect to the endowment effect, they observe no differences in willingness to pay and willingness to accept in either group. Note that the procedures used differ from the ones that commonly find a gap between these two values. 3. Confidence is also similar in that “both groups of subjects display overconfidence at some levels, and neither group shows underconfidence at any level” (p. 82). There is a difference, however, in that older subjects are more accurate. 4. Lottery choices are also very similar across the two groups. In the first task (unknown probabilities), choices evolve toward mostly selecting B for both groups. In the second task (known probabilities), both groups choose from each deck with similar probabilities and, surprisingly, display a slight preference for deck A. There are two other studies of risk preferences in the elderly. Kume and Susuki (2010) compare the behavior of 31 subjects between 65 and 76 years old (from an employment agency in Osaka) to 32 subjects between 25 and 65 (44% are in their 40s), who were employed at the time of the study. The experiment consists of eliciting the willingness to accept for lotteries of a probability p of winning a prize or (1 − p) of getting nothing. The probability is determined randomly for each of the 20 decisions, and the willingness to accept is determined using BDM procedures. The authors report a difference between the two groups; but their analysis ignores statistical significance, making the claims

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difficult to evaluate. Further, the two groups are faced with different lotteries since p is drawn randomly, which also makes it difficult to compare the two groups. Using the summary statistics they report, the following can be said: (1) Both groups are, on average, risk averse, as the willingness to accept is lower than the expected value. (2) The stated willingness to accept is lower for the older group, and this difference is statistically significant at the 1% level.22 Hence, in this data set, the older group seems more risk averse than the younger group. Charness and Villeval (2009) also test for risk preference among older adults. They study junior workers (48, average age 25) and senior workers (39, average age 54) employed in two large private manufacturing companies in France. They also study students (37, average age 21) from schools around Lyon and retirees (35, average age 66) recruited through local associations and one municipality. The task consists of deciding how much of 100 points to invest in a risky asset. The investment fails with probability 50%, in which case the points invested are lost. If it succeeds, then the return is 2.5 times the investment. At the end of the experiment, tokens are converted to Euros at a rate of 40 for 1. A risk-neutral subject should invest everything. The results are as follows: (1) Average behavior in all four groups exhibits some level of risk aversion. (2) There is no statistically significant difference in behavior across groups (average investments range from 50 for students to 59 for the working seniors). If anything, the average moves in the direction of older subjects being less risk averse. Taking the three studies together, it seems that the stereotype that older adults are more risk averse finds little support. In particular, in the one study that finds evidence in that direction (Kume and Suzuki 2010), the older subjects are unemployed and looking for work, whereas the younger subjects are actually not that much younger and are employed. This suggests that their older subjects may be in more immediate need of money. The Charness and Villeval (2009) experiment, however, is mainly aimed at studying cooperation and competition. First, the subjects participate in 17 VCM games in groups of 3 with a MPCR of 0.5. There are 2 blocks of 8, where either the composition of workers (young or old) is known or not known. They conduct sessions in both orders (known, then unknown, and vice versa). This is followed by a seventeenth period where subjects first choose the composition of their group and then play the game. They also conducted a real-effort task where subjects solved anagrams for 4 minutes. Subjects, who were paired, had first to select if they wanted to be paid for the number of anagrams they solved (18 points per anagram) or on the basis of relative performance (30 points per anagram for the winner and 6 points per anagram for the loser). Finally, they elicited beliefs about a subject’s own performance and about the average performance of juniors and seniors. In the VCM game they find that retirees and seniors contribute more than junior workers, and junior workers contribute more than students. They also find that team composition (and its knowledge) affects contributions, namely, heterogeneous groups contribute more. However, in both blocks, contributions trend downward in all groups. This raises the question of whether they may all be trending toward the same (low) contribution level, simply getting there at different speeds. When it comes to competition, behavior is more similar across groups. Subjects in all groups provided more effort (solving anagrams) when they are in a competition rather than when they are paid for absolute performance. Groups do not differ in productivity if they are in a competition. However, retirees are slightly less inclined to choose the tournament than students.

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Holm and Nystedt (2005) perform an experiment through the mail with names they obtained from a public database in Sweden, where they invite 120 subjects, half of whom are 70 and the other half are 20 (in the end, 81 subjects participate). The game is a trust game where player A can send any part of the SEK 100 they received to a player B, the amount sent multiplied by 3. Players also received a flat payment for participating. The main result is an absence of difference between the two groups. They find no statistical difference in the amount sent between the younger and older subjects. They also find no difference in amounts returned, with the mode at one-third of what A sent. However, there is more dispersion in amounts returned in the older group. Besedeš and others (2012) investigate binary lottery choices using 127 subjects in an online study. The subjects are part of a demographically diverse database, maintained at Vanderbilt University, of individuals interested in participating in online experiments. They recruited 35 subjects below 41, 45 subjects above 60, and 47 subjects in the middle group 41 to 60. The task is the following: A card will be drawn from a deck. The number (probabilities) of each card present in the deck is known (the number of cards is varied across rounds, and each card has a different probability of being drawn). Subjects must pick a bet from a prespecified set of options (the number of options is varied). Each option specifies which card would pay. If the subject selected an option that pays out for the card that is drawn, he or she receives $1; otherwise the subject receives nothing. Each subject performs 8 rounds. This problem is one of selecting the option for which the sum of the probabilities where it pays is highest amongst the available options. In other words, in this problem the prize is fixed, and subjects must select the portfolio that pays in the most states of the world, so that an expected utility maximizer would select the option that maximizes the probability that a winning card will be selected, independent of his or her specific utility function. Overall, subjects selected the optimal option 40% of the time, with the frequency of optimal choices decreasing with the number of options, suggesting that complexity decreases performance. On the other hand, there is no significant effect with respect to changing the number of cards over which options are specified. The key result is that performance declines with age: adults over 60 select the optimal choice in 32% of the problems, while this number is 52% for those below 40 (this difference is statistically significant at the 1% level). This represents a 6-percentage-point change in efficiency, from 84% to 90%.23 The small change in efficiency reflects the fact that the cost of mistakes is relatively low in this experiment. They also find that the impact of aging is much less important than that of having a graduate degree. Both in terms of optimality and efficiency, the regressions suggest that not having a graduate degree reduces performance as much as aging by about 40 years. It is difficult to draw overall conclusions about aging given the small number of studies using older adults and the mixed results: some studies find differences while others don’t; there are no systematic patterns yet. This is probably because of important differences in the group of older subjects recruited. The unemployed elderly looking for work, the elderly registered as a control group for studies on Alzheimer’s disease, older adults registered to participate in online experiments: these are all potentially very different types of older adults. Furthermore, these subjects are probably very different from a representative sample of the elderly. Hence, to the extent that this type of research is interested in the impact of declining functions in the aging population, a better understanding of variations in behavior within the elderly population would be useful. However, it seems fair to say that some of the stereotypes about aging are not supported by the data so far.

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V.A Methodological Notes Since aging might affect males and females differentially, this might be an area of research where keeping track of gender is particularly important when comparing groups of different ages. Moreover, unlike typical lab experiments, where assignment to treatments is done randomly from the subject population and thus gender is on average represented in the same proportions across treatments, it may be that the group of older adults under study has a very different ratio of males to females than among younger adults, because women live longer than men. With older subjects, it is often inconvenient to bring them to a laboratory. Hence, many of the experiments with older adults were performed remotely, that is, either online or through the mail. Although it is still unclear to what extent results from experiments in the laboratory versus online differ, this could potentially be a concern. As a practical example, in laboratory experiments it is common practice to read instructions aloud so that subjects know that other subjects were presented with the same instructions (knowledge of common information). When moving to experiments online or through the mail, this possibility is lost.

VI HIGHLY DEMOGRAPHICALLY VARIED (REPRESENTATIVE) SAMPLE Recently, some authors have attempted to perform experiments on a representative sample of a given population. This has, for the most part, occurred within alreadyrunning surveys. This section will review those papers as well as papers that, although they do not have a representative sample, have a highly demographically varied sample.24 Discussing the two together makes sense because the goal is often to identify the impact of demographics (or other variables) on behavior, something that can be done even if the sample under study is not itself representative. Three studies using representative samples investigate the trust game. Fehr and others (2003) use surveys of a representative sample of the adult German population living in private housing. They interviewed 442 individuals, 429 of whom agreed to participate. In their version of the trust game, A players have a finite set of amounts to choose from, and the amount received by the recipient is doubled. Subjects were paid by mail after the answers of players A and B were matched (instead of using the strategy method for B subjects, they randomly give an amount to B based on the probability distribution with which each amount was chosen in a pilot experiment). The second study, Bellemare and Kröger (2007), recruits through the CentERdata, which surveys 2000 households representative of the Dutch population. As in the Fehr and others’ (2003) study, the amount sent by A from a finite set is doubled, but unlike them, they use the strategy method for B’s answer. The third study, Falk and others (2013), uses 1,001 subjects representative of the population of the city of Zurich. Their implementation of the game is similar to that of Bellemare and Kröger (2007), except that the amount sent by the first mover is tripled and they conduct the experiment via mail correspondence.25 All three studies find that very few factors are significant determinants of behavior, with only two factors consistently impacting behavior: age and the beliefs of player A. Not surprisingly, the beliefs of player A regarding what player B will send back correlate positively to the amount sent. With respect to age, although they use different regression specifications, some results overlap. For amount sent, both Bellemare and Kröger (2007) and Falk, Meier, and Zehender (2013) use age and age squared as regressors and find a

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concave relation. Fehr and others (2003) use dummies for blocks of ages and find that adults over 65 give less than those between 35 and 55. Hence, all three studies find that the elderly send less than adults in their midlife. In addition, the specifications of Bellemare and Kröger (2007) and Falk and others imply that the amounts sent increase earlier in life, but Fehr and others do not replicate this finding. Results for amount returned are less homogeneous: Fehr and others report a positive relation to age, Bellemare and Kröger (2007) find a convex relation to age, and Falk and others do not find that age has a significant impact on the amount sent back. In addition, Bellemare and Kröger (2007) and Falk, Meier, and Zehender (2013) also study a standard subject pool of undergraduates (at the University of Tilburg and at the University of Zurich, respectively). Bellemare and Kröger (2007) find that the raw data are statistically different across the two samples. However, the effect is no longer significant once they control for demographics and beliefs. Falk and others, on the other hand, find that the first-mover data is not different across the two samples, with or without demographic controls. The behavior of second movers, however, is different for students and nonstudents (students return less at all amounts, but the slope of the relation is the same). Like Bellemare and Kröger, this is no longer the case once they control for demographic variables. It is not clear how to reconcile the observation that age affects behavior in these three studies with the result of Holm and Nystedt (2005), who find no difference in behavior in the trust game between 20-year-olds and 70-year-olds (see the previous section). It could be that there are differences between the Dutch, Swedish, and Swiss populations. Alternatively, it could be that because the relations between age and behavior are nonlinear, 20- and 70-year olds end up being the same. All three studies also report other demographic factors, beside age, as significant, but those that are significant in one study are not in another, and vice versa. This suggests either false positives, or it could be the result of variations in procedures or in econometric specifications. However, it could also indicate cross-country differences. Another paper using the CentERdata is by Bellemare, Kröger, and van Soest (2008). In that paper they investigate behavior in discrete ultimatum and dictator games. Their game is modified such that no equal-split option is available (the closest offers being 450–550 or 550–450), and the strategy method is used for the responder. Beliefs of proposers were also elicited, although those were not incentivized. A related game, the three-player ultimatum game, is studied by Güth, Schmidt, and Sutter (2007) in a newspaper experiment. The experiment was conducted as a contest in Die Zeit, a well-known news magazine in Germany (1.03 million readers per issue). In total, 25 participants would be randomly selected, with each able to win up to DM 1,000 per person. The 3-player ultimatum game is one where a proposer can select a division of a fixed pie (DM 1,200) between 3 players, in this particular case according to a finite set of options. One of the other 2 players is selected to accept or reject the proposal, while the third (dummy) player accepts whatever he or she has been allocated as in the dictator game. If the proposal is accepted, it determines the final payoffs, and if it is rejected, they all receive nothing. The game is played using the strategy method, with all 3 players choosing in all 3 roles. They were also asked to predict the most common behavior in the role of proposer and responder. Given the specific offers available, (1000, 100, 100) ordered with the proposer first, is the subgame perfect equilibrium (SPE) of the sequential-move game, (400, 400, 400) is the equal split, and (600, 500, 100) is the proposal that comes closest to equalizing payoffs for the proposer and responder while minimizing the payoff to the dummy player. Hence, this game combines the ultimatum

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and dictator games in the sense that the proposer and the one who votes on the offer play an ultimatum game, while the proposer plays a dictator game with the dummy player. Note that the typical results from the ultimatum-dictator games (see Roth 1995) are that in both games, people send positive amounts. In the ultimatum game the mode is close to the equal split, and very little is sent above that. The amounts sent in the dictator game tend to be substantially lower than in the ultimatum game. Finally, in the ultimatum game, offers far below the equal split are rejected more often than almostequal offers. Bellemare, Kröger, and van Soest (2008) find, among many results, that proposer’s beliefs do not correspond to responder behavior. Also, there is substantial heterogeneity, both in behavior and expectations, which cannot be accounted for by observable characteristics. In the three-player ultimatum game of Güth, Schmidt, and Sutter (2007), the findings are that the most common offers are the equal split, followed by the 2-way almost-equal split, and then the SPE offer. Acceptance rates increase with the offer to the person voting and decrease when the proposer’s share is increasing or the dummy’s share is decreasing. When it comes to demographics, there are three results, common to both studies, which stand out, all having to do with age. First, older subjects react more to inequities. In the ultimatum game, the effect of age on proposers is small and mainly shifts the most and second most popular offers from almost equal in favor of the proposer to slightly unequal in favor of the responder. When it comes to responders, both young and old display, on average, a plateau where the probability of acceptance goes down past the almost-equal split point. The slope, in both directions away from the peak, is more pronounced among older subjects. In the 3-player ultimatum game, the frequency of equal splits increases with age, and the frequency of 2-way almost-equal splits decrease with age. On the responder side, the (negative) impact of almost every form of inequity in the distribution becomes more important with age. Second, in both studies, older subjects reject more. It doesn’t matter what it is, even offers as close to equal as possible, older subjects are more likely to reject than younger ones. Third, once you control for age, behavior is similar to that observed in the lab. For the ultimatum game, the preference parameter estimates of the young and highly educated are similar to those of Fehr and Schmidt’s (1999) calibrated distribution based on lab experiments. For the three-player game, controlling for age and education or even simply controlling for age, results are not different from those based on lab experiments reported in Güth and van Damme (1998). In fact, both papers find that the effect of age is more important than that of education. Carpenter, Connolly, and Myers (2008) employ a modified dictator game in which subjects divide $100 between themselves and a charity of their choice (with a 10% chance that their choice will be selected). Some subjects are from a pool of volunteers for experiments at Middlebury College, while the community members were drawn from a sample of 2000 randomly drawn addresses in the state of Vermont.26 The main finding is in line with the other two studies previously mentioned, namely, older people take less for themselves as dictators, and being a student is not a robust determinant of behavior, while age is.27 Besides Güth, Schmidt, and Sutter (2007), others have used newspaper or magazine experiments: Thaler (1997) in the Financial Times (United Kingdom), Bosch-Domènech and Nagel (1997) in Expansión (Spain) and in the Financial Times (United Kingdom), and Nagel and Selten (1997) in Spektrum der Wissenschaft, the

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German edition of Scientific American. All those experiments investigated the beauty contest game. Results from these experiments are discussed in Bosch-Domènech and others (2002). However, unlike Güth and others, those studies did not collect information about demographics, so the impact of these variables cannot be assessed. The key result from these experiments is the presence of spikes at 33.33, 22.22, and 0, with the comments from participants most often describing a logic of iterated best reply. The authors also report that results from experiments with the standard college student subject pool in the laboratory replicate these features except for the spike at 0, which does not exist for the college students. Three more topics that fall in the individual decisions category have been studied in representative samples. First, Huck and Müller (2012) consider the standard Allais paradox choices over lotteries using the previously mentioned CentERdata. They also conduct an experiment using the standard subject pool at the University of Tilburg. The experiment is a between-subjects design with high hypothetical payoffs (millions of Euros), low hypothetical payoffs (up to €25), and low real payoffs. The results can be summarized as follows, in both representative and student samples, Allais-type violations are much more common under high hypothetical payoffs than under low hypothetical payoffs (a difference of 28.2 and 30.6 percentage points for representative and students, respectively, both are statistically significant). Moving from hypothetical small to real small payoffs produces only a small increase in violations (a difference of 4.4 and 3.1 percentage points for representative and students, respectively, with only that for the representative sample being significant).28 Hence, the comparative statics move in the same direction. One important difference, however, is that the number of violations is about 15 percentage points higher for the representative sample in all treatments. The demographics that affect behavior are having a university degree (decrease violations), being employed or self-employed (decrease violations), and having higher income, savings, and assets; all decrease violations. Two other topics that have been investigated using representative samples are risk and intertemporal preferences.29 Andersen and others (2010) uses various modified versions of the Holt-Laury procedure to elicit risk preferences and modified versions of the Coller-Williams procedure to elicit intertemporal preferences.30 They also vary the endowment given to subjects and the order in which various tasks are performed. These are done using students recruited at the University of Copenhagen and the Copenhagen Business School (100 subjects between the ages of 18 and 32) and using a demographically diverse sample of the Danish population (253 subjects between the ages of 19 and 75) that was sampled to be representative.31 The main results are the following: First, there are no statistically significant differences in the average degree of risk aversion between the two samples. The mean coefficient of relative risk aversion (CRRA) is estimated to be 0.63 in the representative sample and 0.79 in the student group. Second, there are no statistically significant differences in average discount rates across the two samples pooled across all horizons (1, 4, and 6 months). Subjects in the representative sample have an average discount rate of 25%, while students average 27.9%. Third, focusing on the representative sample, they identify that adults above 40 are less risk averse than those below, skilled workers are more risk averse, and students are more risk averse. It is somewhat surprising that these factors are significant but that the average CRRA comes out to be almost the same in the student and representative samples. One potential explanation could be that, although the differences cited previously have an impact on risk preferences, they explain but a small fraction of the variance in the CRRA coefficient. Fourth, again for the representative

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sample, none of the demographic variables (such as age, gender, being a parent, etc.) have a statistically significant impact on discount rates. Another study relying on the CentERdata, as well as laboratory experiments by von Gaudecker, van Soest, and Wengström (2012), report very different results. They use a modified Holt-Laury-type procedure, where subjects first choose among four lotteries (presented as pie charts) and then, if they exhibit at most a single switch point, they are presented with an additional screen of four lotteries that allow a more precise estimate of preferences. Payment is in 3 months, and for some options, the outcome is revealed immediately, while for some others it is revealed only in 3 months. In addition, some choices can result in losses (from an endowment so that on net they cannot lose money). There was a high and low real payoff condition as well as a high hypothetical condition. In addition, sessions conducted in the laboratory are implemented in two ways: standard procedures with an experimenter present and one treatment that is closer in format to procedures employed with the CentER subjects. Among the few between-sample results reported, one clear finding is that the standard subject pool makes many fewer mistakes (both with standard methods and with CentER-type methods) than the representative sample. In the standard subject pool, making at least one choice inconsistent with standard models happens 16.2% to 18.4% of the time. For the representative sample the frequency increases to 34.7%. The authors specify a structural model of choice that allows for a form of loss aversion and errors. They report that estimates of risk and loss aversion are smaller, on average, for the typical subject pool. The results of Andersen and others (2010) and von Gaudecker, van Soest, and Wengström (2012) are clearly at odds with these results. One possible explanation suggested by von Gaudecker and others is that they have more data and, thus, more power to distinguish differences. Another possibility seems to be the difference in methods because Andersen and others do not allow subjects to go back and forth in inconsistent ways and, in addition, offer subjects an option to express indifferences. Hence, the difference could be due to how the structural model fits subjects that make “mistakes.” One could imagine, for instance, using the method of von Gaudecker and others, but explaining to subjects why it seems sensible to switch only once. Maybe then the CentERdata would look more like the standard subject pool. In other words, it is not clear that what is picked up by the structural model as a difference in risk preference is actually the expression of a preference. I conclude this section with Belot, Duch, and Miller (2012), who do not use a representative sample but compare students and nonstudents in a laboratory experiment.32 They study the trust game, dictator game, a repeated VCM, a beauty contest, a secondprice auction, and simple choices between an amount for sure and various lotteries to determine risk aversion.33 They report that students are closer to the equilibrium prediction, with standard preferences in all games except for the auction but that the differences are greater for games where other-regarding preferences have a potential role in that students are less other-regarding than the general population.34 They exclude heterogeneity in risk preferences as a potential explanation for these differences based on the fact that both samples exhibit statistically similar behavior in that regard. They also exclude confusion on the basis of two facts. First, differences in behavior are greater in what they consider the simpler other-regarding-preference-related games (they view the dictator game as the simplest, then the trust game, and finally the VCM game). Second, when they control for instruction comprehension (they ask subjects to construct examples and to compute payoffs for those examples), the differences persist. I would point out, however, that when looking at the percentage of subjects

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who understood the instructions, percentage is lower for nonstudents than for students in every single game.35 Combining this with the fact that in the dictator, trust, and VCM games, mistakes are confounded with other-regarding preferences suggests care in interpreting the results. Relatedly, Recalde, Riedl, and Vesterlund (2014) show, using the standard subject pool, evidence that suggests some donations in the VCM game may well be mistakes. When they modify the VCM game to have an interior solution and that solution is for contributions to be low, they obtain the standard result that contributions are above what is predicted in equilibrium (with standard selfish preferences). However, when they modify the game such that the (interior) solution requires high contributions, then subjects on average undercontribute. Hence, by changing the environment, they make confusion go in the direction opposite of what other-regarding preferences predict. This highlights the potential confound and is another indication of the possible increased confusion in the nonstudent subjects of Belot and others. In the VCM game, for both students and nonstudents, Belot, Duch, and Miller (2012) find that repetitions decrease contributions and in both samples, and this happens at what appears to be a similar rate. Hence, although the difference in contributions persists, by the end (in round 10) the difference is no longer statistically significant, with the trend line indicating that any remaining differences will become negligible or completely disappear with more repetitions (since the choice space is bounded from below). The authors also point out that in terms of comparative statics; results are similar for students and nonstudents. In particular, for both samples, repetitions decrease contributions in the VCM, and the frequency of equilibrium play is higher in what they view as the simpler games. As a whole, there are a few patterns that seem to emerge from the use of demographically varied samples. One is that results are often not drastically different from those using the standard sample of student subjects, certainly when it comes to comparative statics, and to the extent that there are differences, these can often be traced to age. Another factor that sometimes has an impact is education. It is unclear, however, why some factors matter some time for some behaviors and not for others. There is no selfevident model of behavior or the role of specific demographic variables that one can see emerging from these studies taken as a whole. However, representative samples sometimes exhibit more “mistakes” (as compared to standard theoretical benchmarks). A couple of possible perspectives on this are that either that the standard subject pool gives a lower bound on the distance between behavior and standard models or that responses from representative samples are noisier. This could result from subjects having a harder time understanding instructions or because they are not incentivized enough. VI.A Methodological Notes Carpenter, Connolly, and Myers (2008) point out that the dictator game is unnatural in the sense that it is a very artificial way of representing donations to charity. Although I agree with that statement, I would like to point out that originally, and in many other studies, the dictator game is not used as a way to understand charitable donations but rather as a tool to decompose the strategic versus altruistic parts of positive offers in the ultimatum game (Forsythe et al. 1994). As such, it would seem undesirable to use it to gain insight into charitable giving.36 One potential issue with using surveys to administer experiments and with using nonstudents to take part in those experiments is that there may be more confusion on

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the part of subjects. For instance, in Fehr and others (2003), the amounts of money returned by the second movers in the trust game is only very weakly correlated to what the first movers sent; and in Güth, Schmidt, and Sutter (2007), older people have a tendency to reject everything more than younger ones. Both these observations could be the result of confusion. Finally, newspaper experiments also have certain specific disadvantages. One is that there may be important selection effects in terms of who reads which paper. Also, newspapers are sometimes unwilling to use neutral frames. In the case of the Güth and others’ (2007) study, this resulted in presenting the problem as one of dividing money between brothers, which has its own specific set of moral judgments attached to it.

VII SUBJECTS WITH RELEVANT TASK EXPERIENCE Experimental studies with professionals, subjects who have experience in the domain of interest, are clearly interesting. Professionals have experience at a task and have been selected in lieu of others to perform it. Take the case of auctions: it seems one could learn a lot from studying professional bidders, and there is one such study that investigates the behavior of professionals from the construction industry in a common value auction. These subjects are interesting because they are the prototypical agent bidding in common value auctions. It is self-evident that people who bid for contracts for a living are auction professionals. However, are expert chess players the prototypical people playing the centipede game?37 That seems less clear, because nobody actually plays the centipede game outside of the laboratory. This game was designed to illuminate certain aspects of strategic interactions: in particular backward induction. It is true that backward induction can be important in chess, and thus one would reason chess players must be good at it; but playing the centipede game is not something at which they are professionals. Similarly, nurses are not professionals at playing the VCM game. They deliver health care, a public good, but hopefully they receive appropriate compensation, and thus they are not the ones bearing the cost of the public good. It may be that nurses are by nature more compassionate, but this is different from saying they are professionals in VCM-type environments. That is why this section is about subjects with relevant task experience; not really professionals. I will use professionals as shorthand, but this is not to imply that these subjects necessarily have professional experience at the game being studied. For the same reason expressed before, I believe our perspective on these experiments should be somewhat nuanced. If I learn that expert chess players all stop in the first move of the centipede game, that does not mean that professionals (businessman, traders, auction bidders, developers, bureaucrats, etc.) are rational. Students are not representative of the group of interest in some ways, but expert chess players are not representative either. Both groups are interesting, and our understanding of rationality, of the extent to which humans perform backward induction, and of the role of common knowledge of rationality depends on whether we find similar results or different results in these two samples. However, one does not invalidate the other, nor does a sample of such “professionals” provide more-direct evidence about the rationality of people who engage in economic activity than the behavior of students. The first study to compare professionals to the usual subject pool of undergraduate students in an economic experiment is, to the best of my knowledge, due to Fouraker,

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Siegel, and Hartnett (1962). They compare bargaining game behavior of students with that of sales division employees from General Electric. However, the first paper of this sort to appear in an economics volume was published much later, in 1985, and it studied wool buyers in an oral double auction. This was followed by DeJong, Forsythe, and Uechker (1988) comparing students to accounting or auditing partners and corporate financial officers in a principal-agent problem. The experiment by Fouraker and others incentivized each group at different rates, although there is no mention of how these rates compared to the opportunity cost of their respective groups. The next two papers (Burns 1985; DeJong, Forsythe, and Uechker 1988) had unusual incentives (either for both groups of subjects or at least for the group of professionals), and, as such, any difference in behavior could be the result of different incentive schemes. Beside these first three papers, the other papers that compare professionals to subjects in standard laboratory studies typically (with the exception of one) have one of two structures for compensation: students and professionals are paid the same or professionals are paid more than students. Fréchette (2015) surveys in detail all studies that conduct treatments with undergraduate students and professionals using standard laboratory procedures with the goal of testing economic theories, which amounts to 13 papers.38 Instead of covering all these papers in detail, I will summarize Burns (1985) as a representative of the early wave of studies (with unusual incentives). Then I will summarize a more recent paper by Cooper and others (1999), which provides the most serious attempt at controlling incentives across groups. These two papers will illustrate one of the most interesting results to come out of this literature. The other papers will be very briefly described; the interested reader is referred to Fréchette (2015) for more details.39 In addition, experiments with professionals that can be compared to experiments with students, even if the two were not both conducted by the same authors or with the same procedures, are covered here.40 Burns (1985) compares 9 student subjects (second-year microeconomics undergraduates) to 9 experienced wool buyers. They are both asked to bid as buyers on 2 units in a progressive oral auction with homogeneous commodities and fixed supply. The progressive oral auction with homogeneous commodities is close to the market in which the wool buyers operate. As a way to stimulate trades, Burns introduced penalties for untraded units; she argues that the requirement to meet the full demand quota is very serious in the wool market. Fifteen auctions were conducted in total (5 per week). Conditions were constant within week, but demand changed across weeks. The experiment was part of a course exercise for which an essay worth 10% of the students’ final assessment must be written. The students did not know the subject of the essay, but they were advised that “only by striving to maximize their profits would they gain the understanding necessary to successfully complete the assignment.” For the wool buyers, it was announced that the “best” trader would be revealed at the end of the session. The data reveal that wool buyers bid up to their marginal values on the first lot and then marginal value plus penalty on the second. On the other hand, students behave similarly to wool buyers on day 1 of week 1, but then the demand curve flattens out in subsequent days (more contracts at or close to the market equilibrium prediction). Thus the students’ behavior is closer to the competitive equilibrium prediction. As a result, students made much more money than wool buyers. When demand conditions changed, both students and wool buyers changed their behavior in the expected direction.

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Discussions and interviews with the wool buyers suggest that their behavior was driven by the behavior they have learned in the market they know. More specifically, wool is not a homogeneous good. Hence, these traders are not accustomed to noticing within-day price variations as these can represent different quality wool. As a result, despite the fact that each auction featured a sharp decline in prices in the course of the session, 7 of the 9 professional buyers reported not noticing that pattern. Cooper et al. (1999) compare Chinese students (10 sessions) to managers from the Chinese textile industry (12 sessions). They compared the behavior of these groups in a standard signaling game which is thought to represent a typical problem in centrally planned economies, namely, the fact that production targets assigned by the central planner to specific firms increase with productivity (the ratchet effect), thus giving an incentive to firms to misrepresent their true productivity. Some sessions were conducted in generic terms, others employed meaningful context (referring to easy and tough contracts, high-productivity firms, etc.). The game was repeated 36 times with roles reversed (“central planners” or “firms”) after every 6 games. The game has three pure-strategy sequential equilibria: pooling at output levels 1, 2, or 3. The students had two payment schedules. In the standard pay: pooling at 2 corresponds to an expected payoff of 30 yuan ($3.75) in each game, which is equivalent to earnings in a typical US experiment. In the high-pay cases, payments were multiplied by 5, which represents 150 yuan in each game with pooling. As a point of comparison, the monthly wage for an associate professor was 1200 yuan. Managers had the same incentives as the students in the high-pay condition. Note that the vast majority of managers in the experiment earned less than 2,000 yuan per month. Overall, firm’s choices start clustered around their type’s full-information output (they are not pooling, but rather acting myopically, not accounting for central planners’ responses to their choices). Central planners give easier contracts to outputs 1 to 3 than higher outputs. Experience increases the frequency of pooling by high-productivity firms (strategic play), with play converging to output level 2. However, a sizable frequency of nonstrategic play by high productivity firms remains even in the last 12 games. For students, increased pay promoted more strategic play by firms initially. However, by the end, there were no differences. Increased pay had no impact on the central planners’ choices. Finally, there are no effects of context on students acting as firms. Mistakes by central planners are reduced for students but only in standard pay. There is an increased level of strategic play for managers in their role as firms in later cycles of play. There is a strong effect on managers as central planners, promoting higher target-rate differentials than in the generic sessions. To summarize, similar behavior is observed between students and managers. However, context helps managers come closer to the pooling equilibrium outcome. The preceding two studies illustrate an important finding that emerges from the review in Fréchette (2015): to the extent that there are differences between professionals and students, these are often the result of aspects of the professional’s work environment that are absent from the game being tested in the laboratory. The professionals either assume that features of their work environment are present in the lab when they are not or they rely on cues that can be triggered only by context. Consequently, these differences do not necessarily make the professionals behave more in line with the theory: sometimes they respond to elements relevant in their work but not in the particular setting being tested. The papers reviewed in Fréchette (2015) are grouped under four broad headings: other-regarding preferences, market experiments, information signals, and a

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miscellaneous group. Other-regarding preferences includes four papers, the oldest being the bargaining experiment from Fouraker and others (1962), using employees of the Industrial Sales Operation division of General Electric. For both professionals and students, when both sides are informed of the profits the other side makes, results are further from the equilibrium and closer to the equal split. Cadsby and Maynes (1998) compare nurses to students in a threshold public goods game.41 The results in this case are very different. Subjects start with total contributions close to the threshold, but as they gain experience their contributions average much lower than the threshold. Nurses, on the other hand, start high above the threshold and finish close to threshold. Fehr and List (2004) use CEOs from the coffee-mill sector in Costa Rica to play a trust game. The main results are that both CEOs and students send money when they are the first mover and ask for the second mover to send back less than the value of the amount sent (three times the original transfer). In both treatments, second movers send back money, and in both cases it averages less than what the first mover asked for. CEOs differ from students in that they send more money when they are first movers (hence they are further away from the equilibrium prediction).42 Carpenter and Seki (2010) study Japanese shrimp fishermen, some of whom work in boats that share all expenses and revenue (poolers) and others who do not (nonpoolers), in a VCM game. Both types of fishermen contribute more than students, with the contribution levels of the different types of fishermen not statistically different from one another.43 Hence, as in Fehr and List (2004), professionals are further from the equilibrium than the students. The other market study, besides Burns (1985), is DeJong, Forsythe, and Uecker (1988). They study members of the professional Accounting Council of the Department of Accounting at the University of Iowa in a principal-agent problem. Principals offer a quality of service and price (sealed bid); agents see the offers and choose from whom to obtain their services. The outcome of the service is determined randomly, but if the quality provided is too low, the loss needs to be covered by the principal. Prices, quality of services, and average expected profits are not statistically different when comparing professionals to students. The category information signals include three studies testing models that rely on Bayesian updating. The first paper of this subgroup, Cooper and others (1999), is covered before. The second, Potters and van Winden (2000), investigates the behavior of public-affairs and public-relations officers in a lobbying game: a signaling game with an informed sender and receiver. Many results are comparable for students and professionals, some in line with the theory and some not. Both groups react in the expected directions, given the strategic tensions. However, professionals in the role of senders are closer to equilibrium predictions in terms of how their messages vary with their information. Alevy, Haigh, and List (2007) study an informationcascade game with market professionals from the Chicago Board of Trade’s floor. The results: a majority of choices in both samples are consistent with Bayesian updating; information cascades are realized at similar rates; and earnings are not different. However, professionals are slightly less Bayesian than students. On the other hand, the behavior of students is sensitive to gains and losses, which is not the case for professionals. The four remaining papers covered in Fréchette (2015) fall in the miscellaneous category. Dyer, Kagel, and Levin (1989) compare the behavior of professionals from the construction industry (with at least 20 years of experience, many in bid preparation), to students’ behavior in a first-price sealed-bid common value auction. Behavior of the two groups is similar in most key categories: average profits, percentage of times the

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winner is the one with the most optimistic signal, and percentage of times the winning bid implies expected loses. In other words, both groups exhibit the winner’s curse. Palacios-Huerta and Volij (2008) investigate the behavior of professional soccer players in two zero-sum games (where the equilibria are in mixed strategies).44 The argument for considering this group in this task is that penalty kicks require mixing. Both groups (soccer players and students) are fairly close to predicted behavior in terms of aggregate average choice frequencies (although the professionals are even closer than students). However, the way in which their behavior differs is in the independence of the choices across repetitions. Students, unlike soccer players, do not generate random sequences. Abbink and Rockenback (2006) study bank employees from the departments of foreign exchange, security, futures, bonds, and money trade in an option-pricing experiment. Although students react more than professionals to a variable that should not affect their behavior (there are two risky states, the variable they react to is the probability of one state versus the other), their average behavior is closer to equilibrium. Also, with experience, students move closer to equilibrium, while professionals move in the opposite direction. Finally, professionals do not arbitrage as much as students. Cooper (2006) compares the behavior of undergraduates and executive MBAs in a weak-link game where managers can also set bonuses.45 The bonus is costly to the managers but increases the value of efforts to the employee. Employees are always undergraduates and only managers vary. By the end, average minimum efforts, bonuses, and profits are similar for both professionals and students. However, professionals attain these levels quicker than students do. On the basis of these 13 papers, I conclude that professionals do not seem qualitatively different from student in any systematic way. In most studies (9 out of the 13) they react to the forces at play in ways similar to students. In the cases where they differ, they are more often further away from the theory than closer. That is probably not because they are less sophisticated but rather, as the first two studies summarized here highlight, because in their professional environment certain elements are present that are absent in the laboratory.46 There are other experiments with professionals that do not include student controls but share enough features with the typical procedures for them to inform us about robustness. In particular, the case of soccer players in zero-sum games (Palacios-Huerta and Volij 2008) has been revisited in two papers. Wooders (2010) reanalyzes the data of Palacios-Huerta and Volij. He finds that the behavior of soccer players follows nonstationary mixtures over the course of the experiment and that they tend to switch from underplaying to overplaying actions with respect to the minimax prediction. In those respects and in terms of the distribution of action frequencies, he finds that students are actually closer to equilibrium than soccer players.47 Another related study is that of Levitt, List, and Reiley (2010). They also study two zero-sum games (one which overlaps with Palacios-Huerta and Volij (2008)) on a sample of US major league soccer players, a sample of professional poker players, and a sample of world-class bridge players.48 Their result is that the behavior of all groups, students, poker players, bridge players, and soccer players, differs from the minimax predictions. This is true at the aggregate level, the individual level, and in terms of serial dependence. Taking all three studies together, it is difficult to know what to think in terms of the ability of these professionals to behave optimally in these environments. For instance, it could be that Spanish soccer players are much better than American ones are.49

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There are some points worth making, nonetheless. Although the three papers often mention how the frequency of play rejects the hypothesis that subjects mix in the correct proportions, in aggregate, these proportions are relatively close. Given the failures both within and across individuals to play mixed strategies, it is an open question as to what forces are at play that bring the aggregate proportions so close to their predicted values. However, it seems clear that the ability to randomize in a serially uncorrelated way is difficult for most subjects.50 Another group of professionals that has been the subject of study are chess players. Palacios-Huerta and Volij (2009) published a study of expert chess players recruited at international tournaments.51 Their sample is composed of one-time play of the centipede game at the tournament and of laboratory studies where subjects (both chess players and students) perform 10 plays of the centipede game. They find that in both settings, chess players’ behavior, when playing other chess players, is extremely close to the theoretical prediction to take in the first node. In fact, when grand masters are the first players, the game always terminates at the first node. When playing repeatedly, chess players quickly converge to the equilibrium prediction. When chess players move first against students, the game terminates at the first node more often than when students play against students, but not as often as when they play against other chess players. Similarly, when students move first against chess players, the game terminates at the first node more often than when they play against other students. However, in a similar experiment, Levitt and others (2011), who also recruited chess players at international tournaments, find very different results.52 Their chess players are very similar to the standard subject pool of students. In fact, none of their grand masters ever stop at the first node. They also have subjects participate in a game that relies on backward induction but in which failure to follow backward induction has no impact on total payoffs (Race to 100) and find that 60% of the chess players behave in accordance with equilibrium in that game. Of the chess players consistent with backward induction in Race to 100, none stopped at the first node in the centipede game. Two other studies use chess players, Bühren and Frank (2010) and de Sousa, Hollard, and Terracol (2014). In these, chess players play one or more beauty contest games. In both cases, results are far from the Nash equilibrium and close to the results (or even further from equilibrium) of experiments with students. In the case of de Sousa and others, this is true even in beauty contest games with only two players, where the solution is a dominant strategy. Levitt, List, and Sadoff (2011) argue that professionals do not recognize the strategic similarities between the centipede game and chess and this is why it is not surprising that they do not behave in line with equilibrium. To wit, when the game is more directly about backward induction (as in their Race to 100), their behavior is more often in line with equilibrium. This explanation seems difficult to reconcile with the behavior of chess players in the de Sousa and others’ paper, where, in a simple game, even when high-Elo players know they are facing other high-Elo players—and furthermore, even when the game has a dominant strategy—chess players behave similarly to students and relatively far from the equilibrium. It is difficult to know what to take away from these varied results except, maybe, that chess players are professionals at playing chess more than anything else. There seems to be no easy way to reconcile the results of Palacios-Huerta and Volij (2009) and Levitt, List, and Sadoff (2011), except maybe that the discrepancy lies in the details of how the experiments were implemented. In some ways, the results of Bühren and

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Frank (2010) and de Sousa Hollard, and Terracol (2014) seem more consistent with the behavior Levitt and others report in the centipede game, but the same cannot be said of the behavior they observe in the Race to 100. Looking at chess players and soccer players together, I find that explanations for the poor performance of professionals in the lab in certain games but not in others seem plausible in some, but not all, cases. If soccer players are professionals at playing mixed strategies with penalty kicks but cannot employ mixed strategies in an experiment because the environment does not call on their understanding of randomizing, does it mean that if we simply frame the environment as one of a soccer game, then they would get it right? This seems unlikely. Given that many of the failures in this particular case have to do with serial dependence, I would speculate that in the field, data sets do not provide as tight a test of players’ ability to generate serially independent draws. Specifically, it would seem that long sequences of uninterrupted repeated plays in stationary environments between two players over a short period of time does not happen in the field. If anything, the studies with chess and soccer players raise as many questions about what allows professionals to perform well in the field as it does about the ways in which the behavior of professionals and students differ or not in the laboratory. Multiple papers (by John List and coauthors) have explored the behavior of professional sports cards dealers. In List and Lucking-Reiley (2000) they compare the behavior of these dealers (they also study card collectors) in multiunit auctions, either using a uniform-price auction or a Vickrey auction. The most directly relevant study with student subjects is Kagel and Levin (2001), who compare behavior in the uniform-price auction and in a dynamic version of the Vickrey auction.53 As predicted by theory, the Vickrey auction yields more demand reduction (the difference in bids between the first and second unit) than the uniform-price auction for all types of subjects: dealers, collectors, and students. However, unlike Kagel and Levin (2001), List and LuckingReiley (2000) also observe some overbidding by professionals on the first unit in the uniform-price auction. Although these results are interesting, Kagel and Levin show that there are complicating factors to be considered (for a thorough analysis read Kagel and Levin in Chapter 9). List (2003, 2004) studies the endowment effect, also with sports card dealers and collectors, as well as with pin collectors. The first paper is done with sports cards and the second with other goods. The endowment effect, the tendency for individuals to value a good more once it is part of his or her endowment, has been documented in many studies with students.54 Consistent with previous results, List observes a significant endowment effect overall. However, the extent of the endowment effect is negatively correlated to market experience. In particular, for subjects with high trading intensity, 11 or more trades per month, there is absolutely no evidence of an endowment effect.55 The behavior of sports card show participants is investigated again in Gneezy and others (2006). The paper documents a phenomenon that violates most models of risky choices, which they term the uncertainty effect: the valuation of a risky prospect is below the value of the worst possible outcome. This is first established in a series of experiments using the standard subject pool. The experiments with the professionals are administered as a Vickrey auction for a single baseball card (one superior and one inferior) or lotteries over the two cards. The experiment with professionals finds the same robust phenomenon: almost all lotteries they experiment with are valued less than the worst card.

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Thus, it seems that in some cases, such as the sports card traders with the endowment effect, behavioral anomalies are mitigated by experience. However, taking the evidence of professionals as a whole, in many instances, what one would conclude from using students is qualitatively similar to what is observed with professionals. VII.A Methodological Notes Experiments with professionals can be insightful, but they also pose challenges.56 There is a tendency to assume professionals should confirm standard models, that market forces should lead professionals to be unbiased optimizers. That is why some worry that student subjects are uninformative (because they do not have the relevant experience and have not been subject to market forces). Hence, when students and professionals behave the same way in the lab, and it is not in line with our standard models, some conclude that this is because transfer of knowledge across domains is difficult. But then, how do we make sense of the cases where professionals with market experience do behave closer to the standard model than students?57 Why can behavior be transferred in those situations? I think this approach is not particularly useful and rests on problematic assumptions. For many of the professionals studied, it is unclear to what extent marketlike forces correct biases. Think of nurses or chess players: what they do is complicated, and the features of their behavior that are rewarded are not necessarily the ones that would bring their behavior in line with some simple optimizing and unbiased behavior. For example, Pope and Schweitzer (2011) establish that the behavior of professional golfers (including the very best) on the PGA tour exhibit loss aversion. If one accepts that biases (relative to expected utility theory) can exist even among top athletes, then observing violations of minimax by professional soccer players in the lab can be interpreted differently. Maybe the problem is not learning transfer, but rather that the laboratory offers a more stringent test of minimax because it is more precise and observations are better. In addition, in the case of many professionals, the fact that they are professionals does not mean they are necessarily highly sophisticated. All this is to say that we might learn more by exploring the source of differences between professionals and students. As I discuss in Fréchette (2015), following the study of professional bidders in the construction industry where Dyer, Kagel, and Levin (1989) observed the winner’s curse, Dyer and Kagel (1996) interviewed the professionals to understand how it could be that they were successful businesspeople and yet lose money in their experiment.58 An important finding is that the market in which they operate is organized in ways to mitigate problems arising from the winner’s curse. Hence, the problem is important enough to affect the industry in how it operates. If, instead, these authors had assumed that businesspeople could not fall prey to the winner’s curse and that the issue must simply be an inability to transfer their knowledge, we would have missed an important discovery and the confirmation that the winner’s curse is difficult to overcome.

VIII DISCUSSION This discussion will be used to bring together results across subject pools on specific topics that have been studied in multiple samples. First, it will cover topics in individual decisions and then move to games, many having some connection to other-regarding preferences.59

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VIII.A Individual Choice Overall, the data suggest that GARP is alive and well, but it also indicates that it is learned. Harbaugh, Krause, and Vesterlund (2001), who include a treatment with undergraduate students, report that in the standard subject pool, the vast majority of choices are in line with GARP.60 Similarly, they also report that young children (ages 7 and 11) display relatively low rates of violations, although the violations decrease with age. This result is confirmed in List and Millimet (2008), who also find that, using a sample of subjects between 6 and 17 years old, violations of GARP decrease with age. Adults in a token economy display choices for the most part consistent with GARP (Battalio et al. 1973). Finally, the behavior of rats, pigeons, and monkeys is broadly consistent with GARP (Kagel et al. 1975; Battalio et al. 1981; Chen, Laksjminarayanan, and Santos 2006), the exception being pigeons who face multiple price changes, although they do move in the right direction. Procedures and tasks vary so much between experiments considering risk preferences that it is difficult to draw general conclusions, in particular, given the focus on point estimates (as opposed to comparative statics). Looking at rats (Battalio, Kagel, and Reynolds 1985), samples of adults of various ages (including the standard subject pool), as well as demographically varied subjects (Kovalchik et al., 2005; Kume and Suzuki 2010; Charness and Villeval 2009; Harrison, Lau, and Rutström 2007), reveals a general tendency toward risk aversion, both across species and within humans; but no clear patterns relating age to risk preferences emerges. Violations of EUT in the Allais paradox are observed in multiple samples: nonhuman animals (Kagel, MacDonald, and Battalio 1990; MacDonald, Kagel, and Battalio 1991), in representative samples, and in the standard subject pool (Huck and Müller 2012). However, the frequency of these violations is much lower in humans when the amounts are low, as compared to the original Allais example in the millions. Furthermore, subjects with a university education exhibit fewer violations. I will loosely discuss, in the same paragraph, prospect theory, reference dependence, loss aversion, and the endowment effect. Although these are distinct concepts, prospect theory, which includes reference dependence and loss aversion, is often given as an explanation of the endowment effect. Evidence consistent with prospect theory and the endowment effect has been documented in multiple studies using undergraduate students (see Barberis (2013) for a review of some of this evidence). However, as we noted previously, Plott and Zeiler (2005) show that evidence on the endowment effect is sensitive to procedures. Notwithstanding this, overall there seem to be multiple instances of behavior consistent with prospect theory and the endowment effect. In line with this, Chen, Lakshminarayanan, and Santos (2006) find evidence consistent with both reference dependence and loss aversion in monkeys. Harbaugh and others find the endowment effect in kindergarteners, third graders, fifth graders, and undergraduate students. Furthermore, it is exhibited to the same extent at all ages. On the other hand, using Plott and Zeiler’s (2005) procedures, Kovalchik and others (2005) find no evidence of the endowment effect in college students nor in adults between 70 and 95 years old. List (2003, 2004) observes the endowment effect, but it disappears in subjects with intense market experience.61 Overall, it seems that there is a tendency, shared across species, to exhibit the endowment effect but that procedures and market experience can make it go away. However, to put this result in perspective, it is interesting to mention the study of Englemann and Hollard (2010). They note that the endowment effect could be the result

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of subjects being uncertain about market procedures, a phenomenon separate from uncertainty over the value of an object. Their experiment introduces a treatment where subjects are forced to trade in three consecutive rounds (otherwise they lose the value of the item they are endowed with) in order for them to learn about market procedures. Subjects who first go through these three rounds do not display the endowment effect. From his experiments, List (2004, 624) concludes, “This result is consistent with the notion that via previous market interaction and arbitrage opportunities, agents have learned to treat goods leaving their endowment as an opportunity cost rather than a loss.” First, note that, although this might be the case, market experience seems to be a rather inefficient teacher because it takes only three trials in the lab to get as much experience as professionals with years of intense trading. Second, the results of Plott and Zeiler (2005) and of Englemann and Hollard (2010) taken together point instead toward individuals learning about market procedures. This is not to say that the endowment effect is not an important phenomenon, but rather that it might be the expression of something different from what it is typically assumed to be. With respect to time preference, two findings are robust across subject pools. First, Andersen and others (2010) find that discount rates are not statistically different between students and a representative sample of the Danish population. Second, Kagel and Green (1987) and Bettinger and Slonim (2007) report behavior consistent with hyperbolic discounting in pigeons and children, respectively. Many studies have observed hyperbolic discounting in student samples; however, some have argued that hyperbolic discounting for laboratory choices over money make little sense given the fungibility of money. In addition, what might look like present bias could simply be uncertainty over future payments.62 We note that neither of these concerns applies to animals, and the fact that adults can move money around probably does not apply to young children. Hence, overall, hyperbolic discounting seems to be present from a young age—and in other animals beside humans. VIII.B Games In the ultimatum and dictator game, results are similar across samples, namely, children (Harbaugh, Krause, and Liday 2003), representative samples (Bellemare, Kröger, and van Soest 2008), and professionals (Fouraker, Siegel, and Harnett 1962). Just like standard subjects (Roth 1995), they all make offers closer to the equal split than predicted by the subgame-perfect equilibrium in the ultimatum game. Also, as offers decrease, the probability of rejection increases. Furthermore, offers are higher in the ultimatum game than in the dictator game. Harbaugh, Krause, and Liday (2003) suggest that this behavior is, at least in part, learned as both offers and the rejection of low offers increase with age. In the VCM game, the standard results are: above-minimum contributions that react to the MPCR and are decreasing with repetitions (Ledyard 1995). A similar pattern is exhibited by older children (above 11.5 years in Harbaugh and Krause (2000) and 9 to 16 years old in Peters et al. (2004)). However, in children under 11.5 years old, Harbaugh and Krause (2000) do not find decreasing contributions when the task is repeated. The above-minimum contribution that decreases with repetitions is also observed in a sample of nonstudent subjects (Belot, Duch, and Miller 2012) and among different types of professionals: the junior and senior workers in manufacturing in Charness and Villeval (2009) as well as in the fishermen who do not pool resources in Carpenter and Seki (2010). For fishermen who pool revenue and expenses, contributions are above the

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minimum but show no signs of decrease with repetitions (the source of the difference in this case could very well be selection). Overall, behavior seems consistent in most samples in the VCM game; however, some aspects of it might be learned, as indicated by the fact that contributions do not decrease for young children. In the trust game, though there are quantitative variations, many of the qualitative results carry over between populations. First, whether it is children (Harbaugh, Krause, and Vesterlund 2002), older subjects (Holm and Nyatedt 2005), representative samples (Fehr et al. 2003; Bellemare and Kr¯oger 2007) or among CEOs (Fehr and List 2004), on average, a positive amount is sent by the first mover, just like results with undergraduates. Similarly, in all groups, the amount sent back by the second mover is a function of what the first mover gave. Although it is difficult to establish clearly in all these papers, from the summary statistics and figures, it seems as if sending more as a first mover increases the return but not enough, on average, to compensate for the loss. Taken together, the evidence seems to point to a concave relation between age and the amount sent by the first mover. The impact of age on second movers is not as clear: some find that it matters, but do not find a consistent relation; others report no differences with age. Some aspects of the beauty contest game seem to generalize across samples. In particular, be it older people (Kovalchik et al. 2005), diverse subjects via newspapers (Nagel and Selten 1998; Thaler 1997; Bosch-Domènech et al. 2002), or chess players (Bühren and Frank 2010; de Sousa, Hollard, and Rerracol 2014), in no case is the winning number ever the equilibrium of zero. Furthermore, many authors report spikes at 22.22 and 33.33 (some do not mention if there are spikes or not). All these patterns are consistent with what is observed in the standard subject pool (Bosch-Domènech et al. 2002; Kovalchik et al. 2005). However, the newspaper experiments also reveal a spike at zero and a lower winning number: between 12 and 17, depending on the study, as opposed to about 24 in the typical experiment. For chess players, Bühren and Frank (2010) report a winning number of 21.43 with the guesses of the grand masters slightly above the average for all players. This suggests that time to think (as in the newspaper experiment) might affect responses more than the intellectual sophistication of the subjects.

IX CONCLUSION In most of the cases for which a task or game has been studied in multiple samples, the results are surprisingly consistent. Qualitative results and comparative statics often carry over from professionals to other species, to undergraduate students. Of course there are some exceptions, but they seem to be just that, exceptions to the general rule. In some cases, certain behavior seems to evolve in childhood. In other cases, behaviors are affected by market exposure. However, the effect of market exposure can be replicated fairly quickly in the laboratory, suggesting it is not about market selection but simply about experimentation. When it comes to point estimates, moving across samples the results are a lot more diverse. However, even with respect to point estimates, it is surprising to find that in some cases there are far fewer (or less obvious) differences than one would have expected—for instance, the similar risk taking behavior for young and old adults. There is no doubt much to be learned from exploring samples besides undergraduate students. In particular, such studies are needed to understand to what extent our typical

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subject pool puts limits, if any, on the type of questions we can explore with some level of confidence and on the factors that affect the robustness of the results. This being said, looking at these studies together gives more confidence than worry about what can be learned from the typical subject pool. In particular, cases where treatment effects (or comparative statics) are different when considering the standard subjects as opposed to other subjects are extremely rare. This also underscores the desirability of focusing on comparative statics. In particular, some of these studies remind us that using the laboratory to estimate preference parameters in designs where mistakes and nonstandard preferences move in the same direction (away from predictions for perfectly optimizing and selfish agents) can be problematic. This can be a serious problem, especially when interpreting results across subject pools. In some ways, these studies highlight many of the advantages from using student subjects: They make replication easier, are less costly, and are easily accessible. Students, by their training, find it easier to understand abstract written instructions. Finally, students, unlike professionals, are less likely to import irrelevant experiences and heuristics into the study, factors that may matter in the setting they typically operate in, but not in the environment under investigation.

ACKNOWLEDGMENTS I wish to thank Jacopo Perego for his tremendous help and comments as well as Guillaume Hollard, John Kagel, Kenway Louie, Andrew Schotter, Emanuel Vespa, and Alistair Wilson for their feedback. I gratefully acknowledge the support of NSF via grants SES-0924780 and SES-1225779 as well as support from the Center for Experimental Social Science (CESS) and the C.V. Starr Center. Its contents are solely the responsibility of the author and do not necessarily represent the official views of the NSF.

NOTES 1. I use infrahuman in the narrow sense of nonhuman animal. 2. A related but distinct issue is whether subjects who volunteer for experiments are different from others who do not. The issue of volunteer artifact in an experiment on electricity demand (how it is affected by changes in prices and other factors) is explored in Kagel, Battalio, and Walker. (1979). See also Falk, Meier, and Zehnder (2013), described in Section VI. 3. This is in addition to the more mundane fact that such experiments are often not conducted in the lab, which can limit what one can do and control. This is true also of experiments with representative samples that are sometimes not administered in the presence of an experimenter, but instead online. 4. One should not read too much in this order. I imagine some patients in the token economies are much further from the subjects we want to study than some children are. But it provides a framework. Note also that representative samples and professionals are not seen as ordered by importance. Their relevance depends on the question of interest. 5. Think of how many experiments with animals must exist on topics relating to economics. 6. This review is very much in the spirit of Ball and Cech (1996). In addition to the types of groups considered here, they also study robustness within the standard subject pool. That is, they consider how results change by educational institution, gender, culture, and so on. 7. Roth (1995) places the beginning of experiments much earlier than what we think of as “modern” experimental economics. 8. It seems unlikely that animals consciously choose consumption bundles by figuring out the point where their indifference curve is parallel to their budget constraints. In that sense, our models are as-if; they are not descriptive models of the choice process.

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9. See, for instance, Rachlin et al. (1980, 1981). 10. A number of the procedures and equipment for running these experiments were adapted from animal experiments in psychology. 11. In typical observational data sets, most variables suffer from some level of measurement error. The same is not true of experimental data with humans or otherwise. However, when it comes to human experiments, income and consumption outside of the experiment suffers from the same potential problems as survey data. 12. The variations have to do with possible confounds due to the procedures; for instance, they change from an open to a closed economy. Other changes in procedures are to address alternative explanations from reinforcement psychology. 13. Results vary with rats depending on procedures, going from choosing exclusively the dominant option (in a simple maze with forced choice) to a very small preference for the dominant option (one of the treatments conducted by Kagel, Battalio, and Green using their type of procedures; for a more complete description see Kagel, Battalio, and Green (1995). 14. The paper by Peters, Ünür, Clark, and Schulze existed as a working paper at least as early as 1997 but was not published until 2004. 15. Group contributions are multiplied by a certain factor; the MPCR is that factor divided by the number of players. 16. Bettinger and Slonim (2006) study the choices of children in a dictator game and analyze the impact of a natural experiment on their behavior. 17. Harbaugh, Krause, and Vesterlund (2007) report that children from age 8 to 18 make offers close to optimal given responder behavior. 18. The Afriat index measures of how much the budget constraint would need to be relaxed to accommodate the choices being consistent with GARP—no violations result in an index of 1. 19. In addition, the paper reports the results of a market experiment with children not summarized here. 20. The policy question motivating this experiment was the potential negative effect of legalizing cannabis on worker incentives. In this respect, one of the most interesting side effects reported is that in one session, subjects went on strike against having to smoke so much pot as it interfered with their earnings from belt making, which was theirs on leaving the experiment. 21. In the cannabis economy subjects were between 20 and 28 years old, as opposed to 19 to 64 years old in Islip. 22. I computed this using the reported summary statistics, but as a result, I cannot account for the fact that we have repeated observations for subjects. If there is positive within-subject correlation (due to risk attitudes, for instance), the standard deviation reported would be too small and the p-value reported too low. 23. Efficiency is computed as the ratio of the expected payoffs of the actual choices to the expected payoffs of the optimal choices. 24. Note also that even studies that aim to have a representative sample do not necessarily end up with a representative sample. 25. Falk, Meier, and Zehnder (2013) also analyze the volunteer artifact by studying donations to a social fund at the University of Zurich by all students who register to the university for the first time over a period of 6 years (16,666 students). Students are asked for these donations at the beginning of each semester, and the fund is used to support foreign students and provide loans for the needy. They find that, although subjects who volunteer to participate in experiments (1,783 of those students) differ from those who do not in terms of their demographics, their donations to that charity are no different. This is true with or without controlling for demographics. 26. Random except with respect to gender because this sample was part of a larger study where males needed to be oversampled. 27. Bekkers (2007) also reports (for a large Dutch sample) that donations to a charity in a dictator game increase with age, but that overall donations are very low. 28. Note that the representative sample is more than six times the size of the student sample, and thus the test has much more power. In fact, when the representative sample is broken down into subgroups of demographics (by age groups, education level, etc.), the difference is no longer significant in 19 of the 29 cases considered. 29. Beside the studies described here, I am aware of two other studies of risk preferences in a representative sample: Dohmen et al. (2011) and Harrison, Lau, and Rutström (2007). The first uses a representative sample of the German population, but their focus is on correlating a survey measure of risk to the standard experimental measure of risk. The second is based on the same sample as in Andersen et al. (2010) that I cover here in more detail.

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Chapter 7 30. Both methods ask subjects a series of binary choices (Coller and Williams 1999; Holt and Laury 2002). 31. Although the sampling method was intended to generate a representative sample, the authors observe sample selection in the subjects who participated in the experiment. 32. The nonstudent subjects were recruited via e-mail to nonacademic staff working at the university, by contacting local shops in Oxford, and by placing advertisements in a local newspaper and in local pubs. 33. Gächter, Herrmann, and Thöni (2004) conduct a one-shot VCM experiment with students and nonstudents in rural and urban Russia. They find that nonstudents contribute more, but none of the multiple demographic variables they consider has a significant effect on contributions. 34. See Cooper and Kagel (Chapter 4) for comparisons of student samples with more representative samples with respect to other-regarding preferences. 35. I would also note that understanding the strategic considerations of a game is more than simply being capable of computing payoffs. 36. Cooper and Kagel (Chapter 4) detail the instabilities in the dictator game—while also pointing out its value for clarifying motives for behavior in the ultimatum game. 37. In the centipede game, introduced by Rosenthal (1981), players take turns choosing either to stop the game or continue. At every node, the player who chooses would make less money if he continued and the other player immediately stopped; but he would make more money if the game continued past that point. The unique subgame perfect Nash equilibrium involves both players defecting at every node at which it is their turn to choose. 38. Fréchette (2015) is only one of the multiple chapters in Fréchette and Schotter (2015) discussing field and laboratory experiments. The interested reader is referred to Chapters 14–20 of that book. 39. In that piece I also explain aspects of the validity of an inference and elaborate on the reasons to study professionals. 40. Some very interesting experimental studies of professionals that have no direct counterparts with students (either in topic or in their implementation) are not included here. These include, for instance: the study of social connections and the impact of managerial incentives in a fruit-picking farm (Bandiera, Barankay, and Rasul 2009), the possibility for gift exchange in a tree-planting firm (Bellemare and Shearer 2009), gender discrimination by taxi drivers (Castillo et al. 2013), and many others. 41. As opposed to a VCM game, the public good is provided only if there is a certain level of contributions; this game has multiple equilibria, one with no contributions and many that have just enough contributions for the public good to be provided. 42. There is also a treatment manipulation, but it has only a small impact on behavior. 43. The paper also explores a modification of the VCM game that allows subjects to express their emotions. 44. The soccer players are from the Spanish division 1 and division 2. In addition to these and a sample of undergraduates with no soccer experience, they also have a sample of undergraduates who currently play in an official amateur senior regional league. 45. In the weak-link, or minimum, game, employees pick costly effort and their profits increase as the minimum of the group increases such that any tuple of efforts that is identical for all employees is an equilibrium, and these are Pareto ranked. 46. Two more recent studies that include professionals and students are Roth and Voskort (2014) and Beck et al. (2014). I will not describe either in detail as they apply to games that have not been widely studied. However, they both report qualitative similarities and quantitative differences between the two samples. 47. The main difference in how the data are analyzed is that Wooders (2010) considers the first and second half of the data separately. 48. They note that using mixed strategies has no role in bridge, while it is an important part of poker. 49. One difficulty in making this argument, however, is that in the Palacios-Huerta and Volij (2008) data, the behavior of the undergraduate students who were amateur players is at least as close or closer to equilibrium than that of the professionals. 50. Note that this is not an intrinsic feature of minimax, since a zero-sum game can be played only once. 51. Chess players are ranked by Elo ratings. The difference in ratings between two players predicts the probability that each will win. Their sample is composed of players with ratings above 2000. 52. Some of their players have Elo ratings below 2000, but most are above. 53. The setting in Kagel and Levin (2001) is simpler for bidders as each human bidder interacts with computerized opponents who have single-unit demand. 54. However, Plott and Zeiler (2005) show that changing instructions and procedures can decrease or even eliminate the endowment effect. 55. Although this is for all samples combined, dealers are the ones with the highest trading intensity. The papers do not report how many years of experience subjects who trade 11 or more times per month have, but from the summary statistics it would seem to be multiple years.

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56. See the multiple chapters discussing the field and lab experiments in Fréchette and Schotter (2015). 57. Even if professionals do not transfer knowledge, how do we make sense of the cases where professionals are further away from equilibrium and make less money on average than students? 58. In the same spirit, Burns (1985) explores the reasons for the professionals’ behavior in her experiment. 59. See Cooper and Kagel (Chapter 4) for comparisons of student samples with more representative samples with respect to other-regarding preferences. 60. The reader interested in a more complete review of the empirical evidence on GARP is referred to Varian (2006) and Andreoni, Gillen, and Harbaugh (2013). 61. Although not reviewed here, note also that List and Haigh (2010) find that the behavior of futures and options pit traders from the Chicago Board of Trade is closer to myopic loss aversion than the behavior of students. 62. See, for instance, Augenblick, Niederle, and Sprenger (2013) for a discussion of these issues and an experiment that addresses them where they show hyperbolic discounting over nonmonetary rewards.

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Burns, Penny. 1985. Experience and Decision Making: A Comparison of Students and Businessmen in a Simulated Progressive Auction. In Research in Experimental Economics, Vol. 3. Greenwich, CT: JAI Press: 139–53. Cadsby, C. Bram, and Elizabeth Maynes. 1998. Choosing between a Socially Efficient and FreeRiding Equilibrium: Nurses versus Economics and Business Students. Journal of Economic Behavior & Organization 37(2): 183–92. Carpenter, Jeffrey, Cristina Connolly, and Caitlin Myers. 2008. Altruistic Behavior in a Representative Dictator Experiment. Experimental Economics 11(3): 282–98. Carpenter, Jeffrey, and Erika Seki. 2010. Do Social Preferences Increase Productivity? Field Experimental Evidence from Fishermen in Toyama Bay. Economic Inquiry 49(2): 612–30. Castillo, Marco, Ragan Petrie, Maximo Torero, and Lise Vesterlund. Forthcoming. Gender Differences in Bargaining Outcomes: A Field Experiment on Discrimination. Journal of Public Economics. Charness, Gary, Guillaume R. Fréchette, and John H. Kagel. 2004. How Robust is Laboratory Gift Exchange? Experimental Economics 7(2): 189–205. Charness, Gary, and Marie-Claire Villeval. 2009. Cooperation and Competition in Intergenerational Experiments in the Field and the Laboratory. American Economic Review 99(3): 956–78 Chen, M. Keith, Venkat Lakshminarayanan, and Laurie R. Santos. 2006. How Basic Are Behavioral Biases? Evidence from Capuchin Monkey Trading Behavior. Journal of Political Economy 114(3): 517–37. Coller, Maribeth, and Melonie B. Williams. 1999. Eliciting Individual Discount Rates. Experimental Economics 2(2): 107–27. Cooper, David J. 2006. Are Experienced Managers Experts at Overcoming Coordination Failure? The B.E. Journal of Economic Analysis & Policy 5(2). Cooper, David J., John H. Kagel, Wei Lo, and Qing Liang Gu. 1999. Gaming Against Managers in Incentive Systems: Experimental Results with Chinese Students and Chinese Managers. American Economic Review 89: 781–804. Cox, James C. 1997. On Testing the Utility Hypothesis. The Economic Journal, 107(443): 1054–78. de Sousa, Jose, Guillaume Hollard, and Antoine Terracol. 2014. Non-Strategic Players Are the Rule Rather Than the Exception. Working paper. DeJong, Douglas V., Robert Forsythe, and Wilfred C. Uecker. 1988. A Note On The Use of Businessmen as Subjects in Sealed Offer Markets. Journal of Economic Behavior and Organization 9: 87–100. Dohmen, Thomas J., Armin Falk, David Huffman, Jürgen Schupp, Uwe Sunde, and Gert Georg Wagner. 2011. Individual Risk Attitudes: Measurement, Determinants and Behavioral Consequences. Journal of the European Economic Association 9(3): 522–50. Dyer, Douglas, and John H. Kagel. 1996. Bidding in Common Value Auctions: How the Commercial Construction Industry Corrects for the Winner’s Curse. Management Science 42(10): 1463–75. Dyer, Douglas, John H. Kagel, and Dan Levin. 1989. A Comparison of Naïve and Experienced Bidder in Common Value Offer Auctions: A Laboratory Analysis. The Economic Journal 99: 108–15. Englemann, Dirk, and Guillaume Hollard. 2010. Reconsidering the Effect of Market Experience on the “Endowment Effect.” Econometrica 78(6): 2005–19. Falk, Armin, Stephan Meier, and Christian Zehnder. 2013. Do Lab Experiments Misrepresent Social Preferences? The Case of Self-Selected Student Samples. Journal of the European Economic Association 11(4): 839–52. Fehr, Ernst, Urs Fischbacher, Jürgen Schupp, Bernhard von Rosenbladt, and Gert Georg Wagner. 2003. A Nationwide Laboratory Examining Trust and Trustworthiness by Integrating Behavioural Experiments into Representative Surveys. IEW working paper No. 141.

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Chapter 7 Fehr, Ernst, and John A. List. 2004. The Hidden Costs and Returns of Incentives—Trust and Trustworthiness among CEOs. Journal of the European Economic Association 2(5): 743–71. Fehr, Ernst, and Klaus M. Schmidt. 1999. A Theory of Fairness, Competition, and Cooperation. Quarterly Journal of Economics 114(3): 817–68. Forsythe, Robert, Joel L. Horowitz, N. E. Savin, and Martin Sefton. 1994. Fairness in Simple Bargaining Experiments. Games and Economic Behavior 6: 347–69. Fouraker, Lawrence E., Sidney Siegel, and D. L. Harnett. 1962. An Experimental Disposition of Alternative Bilateral Monopoly Models Under Conditions of Price Leadership. Operations Research 10(1): 41–50. Fréchette, Guillaume R. 2015. Laboratory Experiments: Professionals versus Students. In Guillaume Fréchette and Andrew Schotter, The Methods of Modern Experimental Economics. New York: Oxford University Press, 360–90. Fréchette, Guillaume R., and Andrew Schotter, eds. 2015. The Methods of Modern Experimental Economics. New York: Oxford University Press. Frederick, Shane, George Loewenstein, and Ted O’ Donoghue. 2002. Time Discounting and Time Preference: A Critical Review. Journal of Economic Literature 40: 350–401. Gächter Simon, Benedikt Herrmann, Christian Thöni. 2004. Trust, Voluntary Cooperation, and Socio-Economic Background: Survey and Experimental Evidence. Journal of Economic Behavior and Organization 55: 505–31. Gneezy, Uri, John A. List, and George Wu. 2006. The Uncertainty Effect: When a Risky Prospect Is Valued Less than Its Worst Possible Outcome. Quarterly Journal of Economics 121(4): 1283–1309. Güth, Werner, Carsten Schmidt, and Matthias Sutter. 2007. Bargaining Outside the Lab—A Newspaper Experiment of a Three-Person Ultimatum Game. Economic Journal 117(518): 449–69. Güth, Werner, and Eric Van Damme. 1998. Information, strategic behavior, and fairness in ultimatum bargaining: An experimental study. Journal of mathematical Psychology 42(2): 227–47. Harbaugh, William T., and Kate Krause. 2000. Children’s Altruism in Public Good and Dictator Experiments. Economic Inquiry 38(10): 95–109. Harbaugh, William T., Kate Krause, and Timothy R. Berry. 2001. GARP for Kids: On the Development of Rational Choice Behavior. American Economic Review 91(5): 1539–45. Harbaugh, William T., Kate Krause, and Steven G. Liday Jr. 2003. Trust Bargaining by Children. Working paper. Harbaugh, William T., Kate Krause, Steven G. Liday Jr., and Lise Vesterlund. 2002. Trust in Children. Working paper. Harbaugh, William T., Kate Krause, and Lise Vesterlund. 2001. Are Adults Better Behaved Than Children? Age, Experience, and the Endowment Effect. Economics Letters 70(2): 175–81. ———. 2002. Risk Attitudes of Children and Adults: Choices Over Small and Large Probability Gains and Losses. Experimental Economics 5(1): 53–84. ———. 2007. Learning to Bargain. Journal of Economic Psychology 28(1): 127–42. Harrison, Glenn W., Morten I. Lau, and E. Elisabet Rutström. 2007. Estimating Risk Attitudes in Denmark: A Field Experiment. Scandinavian Journal of Economics 109(2): 341–68. Herrnstein, Richard J. 1961. Relative and Absolute Strength of Responses as a Function of Frequency of Reinforcement. Journal of the Experimental Analysis of Behaviour 4: 267–72. Holm, Håkan, and Paul Nystedt. 2005. Intra-Generational Trust—A Semi-Experimental Study of Trust among Different Generations. Journal of Economic Behavior & Organization 58: 403–19. Holt, Charles A., and Susan K. Laury. 2002. Risk Aversion and Incentive Effects. American Economic Review 92(5): 1644–55. Huck, Steffen, and Wieland Müller. 2012. Allais for All: Revisiting the Paradox in a Large Representative Sample. Journal of Risk and Uncertainty 44(3): 261–93.

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Kagel, John H. 1972. Token Economies and Experimental Economics. The Journal of Political Economy 80(4): 779–85. Kagel, John H., Raymond C. Battalio, and Leonard Green. 1995. Economic Choice Theory. Cambridge, UK: Cambridge University Press. Kagel, John H., Raymond C. Battalio, and C. G. Miles. 1980. Marihuana And Work Performance: Results from an Experiment. The Journal of Human Resources 15(3): 373–95. Kagel, John H., Raymond C. Battalio, Howard Rachlin, and Leonard Green. 1981. Demand Curves for Animal Consumers. The Quarterly Journal of Economics 96(1): 1–16. Kagel, John H., Raymond C. Battalio, Howard Rachlin, Leonard Green, Robert Basmann, and W. R. Klemm. 1975. Experimental Studies of Consumer Demand Behavior Using Laboratory Animals. Economic Inquiry 13(1): 22–38. Kagel, John H., Raymond C. Battalio, and James M. Walker. 1979. Volunteer Artifacts in Experiments in Economics: Specification of the Problem and Some Initial Data from a SmallScale Field Experiment. Research in Experimental Economics (1): 169–97. Kagel, John H., Raymond C. Battalio, Robin C. Winkler, and Edwin B. Fisher Jr. 1977. Job Choice and Total Labor Supply: An Experimental Analysis. Southern Economic Journal 44(1): 13–24. Kagel, John H., and Leonard Green. 1987. Intertemporal Choice Behavior: Evaluation of Economic and Psychological Models. In John H. Kagel and Leonard Green, eds., Advances in Behavioral Economics, Vol. 1. Norwood, NJ: Ablex Publishing. Kagel, John H., and Dan Levin. 2001. Behavior in Multi-Unit Demand Auctions: Experiments with Uniform Price and Dynamic Vickrey Auctions. Econometrica 69(2): 413–54. Kagel, John H., Don N. MacDonald, and Raymond C. Battalio. 1990. Tests of “Fanning Out” of Indifference Curves: Results from Animal and Human Experiments. American Economic Review 80(4): 912–21. Kovalchik, Stephanie, Colin F. Camerer, David M. Grether, Charles R. Plott, and John M. Allman. 2005. Aging and Decision Making: A Comparison between Neurologically Healthy Elderly and Young Individuals. Journal of Economic Behavior & Organization 58: 79–94. Kume, Koichi, and Ayako Suzuki. 2010. Ageing, Probability Weighting, and Reference Point Adaptation: Experimental Evidence. Working paper. Ledyard, John O. 1995. Public Goods: A Survey of Experimental Research. In John H. Kagel and Alvin E. Roth, eds., Handbook of Experimental Economics. Princeton, NJ: Princeton University Press, Chapter 2. Levitt, Steven D., John A. List, and David H. Reiley. 2010. What Happens in the Field Stays in the Field: Exploring Whether Professionals Play Minimax in Laboratory Experiments. Econometrica 78(4). Levitt, Steven D., John A. List, and Sally E. Sadoff. 2011. Checkmate: Exploring Backward Induction among Chess Players. American Economic Review 101(2): 975–90. List, John A. 2003. Does Market Experience Eliminate Market Anomalies? Quarterly Journal of Economics 118(1): 41–71. ———. 2004. Neoclassical Theory versus Prospect Theory: Evidence from the Marketplace. Econometrica 72(2): 615–25. List, John A., and Micheal S. Haigh. 2010. Investment under Uncertainty: Testing the Options Model with Professional Traders. Review of Economics and Statistics 92(4): 974–84. List, John A., and David Lucking-Reiley. 2000. Demand Reduction in Multiunit Auctions: Evidence from a Sportscard Field Experiment. American Economic Review 90(4): 961–72. List, John A., and Daniel L. Millimet. 2008. The Market: Catalyst for Rationality and Filter of Irrationality. The B.E. Journal of Economic Analysis & Policy 8(1): 1–55. MacDonald, Don N., John H. Kagel, and Raymond C. Battalio. 1991. Animals’ Choices over Uncertain Outcomes: Further Experimental Results. The Economic Journal 101(408): 1067–84. Machina, Mark J. 1987. Choice under Uncertainty: Problems Solved and Unsolved. Journal of Economic Perspectives 1: 121–54. Madies, Thierry, Marie Claire Villeval, and Malgorzata Wasmer. 2013. Intergenerational Attitudes towards Strategic Uncertainty and Competition: A Field Experiment in a Swiss Bank. European Economic Review 61: 53–168.

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Chapter 7 Nagel, Rosemarie and Reinhard Selten. 1997. 1000 DM zu gewinnen. Spektrum der Wissenschaft (November). Palacios-Huerta, Ignacio, and Oscar Volij. 2008. Experientia Docet: Professionals Play Minimax in Laboratory Experiments. Econometrica 76(1): 71–115. ———. 2009. Field Centipedes. American Economic Review 99(4): 1619–35. Peters, H. Elizabeth, A. Sinan Ünür, Jeremy Clark, and William D. Schulze. 2004. Free-Riding and the Provision of Public Goods in the Family: A Laboratory Experiment. International Economic Review 45(1): 283–99. Plott, Charles R., and Kathryn Zeiler. 2005. The Willingness to Pay–Willingness to Accept Gap, the “Endowment Effect,” Subject Misconceptions, and Experimental Procedures for Eliciting Valuations. The American Economic Review 95(3): 530–45. Pope, Devin G., and Maurice E. Schweitzer. 2011. Is Tiger Woods Loss Averse? Persistent Bias in the Face of Experience, Competition, and High Stakes. American Economic Review 101(1): 129–57. Potters, Jan, and Frans van Winden. 2000. Professionals and Students in a Lobbying Experiment Professional Rules of Conduct and Subject Surrogacy. Journal of Economic Behavior & Organization 43: 499–522. Rachlin, Howard, Raymond. C. Battalio, John H. Kagel, and Leonard Green. 1981. Maximization Theory in Behavioral Psychology. The Behavior and Brain Sciences 4(03): 371–88. Rachlin, Howard, John H. Kagel, and Raymond. C. Battalio. 1980. Substitutability in Time Allocation. Psychological Review 87. Recalde, Maria P., Arno Riedl, and Lise Vesterlund. 2014. Error Prone Inference from Response Time: The Case of Intuitive Generosity. Working paper. Rosenthal, Robert. 1981. Games of Perfect Information, Predatory Pricing, and the Chain Store. Journal of Economic Theory 25(1): 92–100. Roth, Alvin E. 1995. Bargaining Experiments. In John H. Kagel and Alvin E. Roth, eds., Handbook of Experimental Economics. Princeton, NJ: Princeton University Press, Chapter 4. Roth, Benjamin, and Andrea Voskort. Forthcoming. Stereotypes and False Consensus: How Financial Professionals Predict Risk Preferences. Journal of Economic Behavior & Organization. Shafir, Sharoni, Tom A. Waite, and Brian H. Smith. 2002. Context-Dependent Violations of Rational Choice in Honeybees (Apis mellifera) and Gray Jays (Perisoreus canadensis). Behavioral Ecology and Sociobiology 51(2): 180–87. Sutter, Matthias, Peter Martinsson, Francesco Feri, Katarina Nordblom, Martin G. Kocher, and Daniela Rützler. 2010. Social Preferences in Childhood and Adolescence: A Large-Scale Experiment. IZA DP No. 5016. Working paper. Tarr, David G. 1976. Experiments in Token Economies: A Review of the Evidence Relating to Assumptions and Implications of Economic Theory. Southern Economic Journal 43(2): 1136–43. Thaler, Richard H. 1997. Giving Markets a Human Dimension. Financial Times 6(June): 16. Varian, Hal R. 2006. Revealed Preference. In M. Szenberg, L. Ramrattan, and A. A. Gottesman, eds., Samuelson Economics and the Twenty-First Century. Oxford, UK: Oxford University Press, 99–115. von Gaudecker, Hans-Martin, Arthur van Soest, and Erik Wengström. 2012. Experts in Experiments: How Selection Matters for Estimated Distributions of Risk Preferences. Journal of Risk and Uncertainty 45(2): 159–90. Wooders, John. 2010. Does Experience Teach? Professionals and Minimax Play in the Lab. Econometrica 78(3): 1143–54.

8 Gender Muriel Niederle

I INTRODUCTION Gender is deeply rooted in our identity and is one of the first traits we observe about others.1 Gender differences receive enormous attention by the popular press and the public: John Gray’s (1992) book Men are from Mars, Women are from Venus has sold more than 50 million copies and in the 1990s was ranked as the third-most-popular book.2 More recently, Sheryl Sandberg’s (2013) Lean In, a controversial and muchdiscussed book, has spent weeks at the top of best-seller lists. While the psychology literature has debated gender differences in preferences for almost 150 years (Hyde 2005; Shields 1975), the discussion of gender has only recently started to gain momentum in economics. For example, most chapters in the last Handbook of Experimental Economics (Kagel and Roth 1995) did not even mention gender differences—even Ledyard’s chapter on public goods, referencing roughly 250 papers, includes only 6 papers studying gender differences. Since the turn of the millennium, the situation has changed and there has been an explosion of experimental work on gender differences in economics. There are now several surveys focusing solely on that topic (Eckel and Grossman 2008b, 2008c; Croson and Gneezy 2009). In this chapter I revisit the three traits for which gender differences have been most extensively studied: attitudes to competition, altruism or cooperative attitudes, and risk attitudes. In each section I focus on series of experiments and also present early results from the psychology literature (though this literature does not have results for competition). One of the strengths of experimental economics is that many findings are replicated and studied in different contexts to establish whether the initial finding was a true and robust result as opposed to a false-positive or a rather knife-edge result.3 This survey focuses on experiments in which there is little or no interaction between agents. This reduces the influence of confounds such as potential gender differences in strategic behavior or discrimination that may be present in more complex interactions such as sequential or repeated games. While there are many other areas in which gender differences have been documented, I am neglecting these areas not because they lack importance or interest, but rather to keep the chapter at a manageable length.

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Why have economists not studied gender differences in psychological attributes earlier, given the interest in gender differences in economic outcomes? Attributing field evidence of gender differences in outcomes to specific traits is difficult. For example, assessing gender differences in altruism in the field often relies on observing gender differences that cannot be explained by standard economic variables such as socioeconomic status, income, and so on.4 The difficulty of attributing gender differences in labor market outcomes to specific traits may contribute to labor economists focusing on two other possible sources of gender differences: discrimination and differences in human capital accumulation. The latter may either be in the form of education before labor market entry or in the form of accumulated experience after having entered the labor market (see Altonji and Blank’s (1999) “Race and Gender in the Labor Market” in the third volume of Handbook of Labor Economics.) In contrast to field evidence inferring altruism as the unexplained variation of a complex choice that can be the result of many motives, the laboratory can be stripped of many confounding factors, and decisions can be observed in a highly controlled environment. In doing so, we can directly measure traits such as attitudes to competition, altruism, and risk. With the rise of behavioral and experimental economics, the study of gender differences in traits has received growing attention. As my chapter focuses on gender differences, it is worthwhile to note that these differences, while significant, are sometimes small. This has been the case for many psychological traits, and almost since its inception, the literature on gender differences consisted of two camps. One side argues for the existence and importance of gender differences, and the other side emphasizes gender similarities. As an example of the “differences are important” camp, Eckel and Grossman (1998), in their foreword, cite Charles Darwin (1874, 586) “[w]oman seems to differ from man in mental disposition, chiefly in her greater tenderness and less selfishness . . . Man . . . delights in competition, and this leads to ambition which passes too easily into selfishness.” In the “differences are small” camp, Hyde (2005) calls her review on the psychological literature The Gender Similarities Hypothesis. Whether statistically significant gender differences are economically significant, so that it is more appropriate to talk of gender differences rather than gender similarities, depends on the question at hand. In cases where the average outcome of one decision is of interest, small gender differences may not be economically important. However, there are cases in which even small differences can result in significant effects. When studying repeated choices, small differences might accumulate, thereby calling for policy interventions. For example, if the structure of an exam is such that there are penalties for wrong answers, small differences in risk aversion may result in women being, on average, slightly more likely to skip a question than men are. In an exam with many questions, even a small difference can accumulate to generate a more sizable effect. Furthermore, small average differences in normal distributions become larger when assessing the probability of gender representations among participants with extreme versions of that trait. Indeed, there is a long and ongoing debate about gender differences in math ability and the extent to which gender differences are exacerbated among those of very high ability. Recall the heated and very ideological debate that followed Larry Summers’ comments on January 14, 2005, in which he suggested the underrepresentation of female scientists at top universities may be in part due to natural ability differences between men and women. The study of gender differences has, almost since its inception, been plagued by ideologically guided interpretations. In the first review of the literature on gender

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differences in psychology, Woolley (1914) pointed out and deplored the gap between the predominant views on the question, including that of scientists versus the conclusions supported by data. Hyde (2005, 581) cites Woolley (1914, 372): “The general discussions of the psychology of sex, whether by psychologists or by sociologists show such a wide diversity of points of view that one feels that the truest thing to be said at present is that scientific evidence plays very little part in producing convictions.” When surveying gender differences in various traits, I will therefore aim to provide a balanced view and provide interpretation of the magnitude of observed differences. Summarizing the evidence presented in this chapter, I find that there are large gender differences in reaction toward competition, with women shying away from competition with men and women underperforming when competing against men. These differences persist and are only somewhat reduced when controlling for beliefs about relative performance as well as risk aversion. The robust finding is that gender differences are particularly pronounced when performance is measured in tasks that are not stereotypically female. In addition, there is some new evidence that women shy away from challenging tasks and refrain from “speaking up.” The evidence on gender differences in altruism is much more mixed. While some studies find women to be more altruistic than men, this is not always the case, and differences, when they exist, are often small. A more robust conclusion seems to be that women and men differ in how their utility depends on the payoffs of others. Specifically, women seem more concerned with equalizing payoffs among laboratory participants, while men seem to have a higher preference for efficiency; that is, donations by women compared to donations by men respond less to the costs of giving. The behavior in more complex public good games is less amenable to a simple summary, though recent studies have provided promising inroads in understanding the interplay between donations to a public good and strategic reactions toward the way the public good is provided. The evidence on gender differences in risk aversion is also much less clear than one might expect. Some methods of eliciting risk preferences, while showing variation across participants, result in no, or very small, gender differences. Other elicitation methods produce reliable gender differences, with women being more risk averse. It is, however, somewhat disconcerting that different elicitation methods are often not very correlated with one another, and each one seems quite valid in estimating risk preferences. This lack of a unified result could be due to the fact that risk preference in itself is complex and is not easily reducible to the outcome of a single choice. Once gender differences in a trait have been established through extensive replications in different laboratories, it is important to show that these differences can occur outside of the laboratory, beyond experiments with students. One way to do this is with field experiments that can bring “laboratory-style” decisions to the field. Another way is to find an interesting variation that occurred naturally. To date there are at least two summaries of the literature assessing the role of experimental findings on gender differences for labor economics in field settings, Bertrand (2011) and Azmat and Petrongolo (2014). External validity shows that a result—a gender difference in behavior—can be found outside of the laboratory and is not specific to standard student subject pools or standard laboratory tasks and decisions that are simple and short. However, nonlaboratory studies often occur with subject pools that are equally (or perhaps even more) special than undergraduate students. For example, assume a specific gender difference is replicated using Austrian farmers. This result is not necessarily more predictive of behavior of Austrians in general—or American farmers—than the result established in

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the laboratory. Most importantly, finding a gender gap in a given trait among Austrian farmers does not imply that economic differences among Austrian farmers are due to this particular trait. And, of course, it certainly does not inform us that gender differences in economic outcomes among Austrians in general (or American farmers) can be attributed to gender differences in this trait. External validity is exactly that: it shows that a trait is valid outside of a laboratory setting. It does not, however, necessarily tell us if that this trait is relevant for general economic outcomes. In other words, documenting results outside of the laboratory cannot always speak to the broader importance of external relevance. Bertand (2011, 1581) makes this point in the conclusions of her chapter on gender in the labor market for the fourth volume of the Handbook of Labor Economics: “While the laboratory evidence shows in many cases large gender differences (say, in attitudes towards risk, or attitudes towards competition), most of the existing attempts to measure the impact of these factors on actual outcomes fail to find large effects. This is undoubtedly a reflection of a rather new research agenda, as well as of the difficulty in finding databases that combine good measures of psychological attributes with real outcomes. More direct demonstrations of field relevance will be crucial for these new perspectives to have a lasting impact on how labor economists approach their study of gender gaps.” Each section on competition, altruism, and risk will have some evidence regarding the external validity of the laboratory findings through field experiments and naturally occurring data. However, special emphasis will be placed on showing that gender differences in a given trait can account for a significant fraction of gender differences in economic decisions relevant to labor market or education outcomes of women and men. That is, I will try to emphasize the evidence for the external relevance of gender differences in competition, altruism, and risk. After establishing the importance of gender differences in psychological traits for education and labor market outcomes, the question is what to do with this knowledge. A first natural question is whether—or how much—of these differences are due to nature or nurture. If they are due to nurture, maybe these traits can be changed, though this may require a deeper investigation into the potential benefits of doing so. A second question is whether these gender differences are indeed “true” differences in preferences or whether they instead represent biases of women (or men) and whether awareness of those gender differences may therefore act as a way to “debias” the decisions of women and men.5 At heart, this is one of the messages of Sandberg’s (2013) Lean In. Another possible next step is to assess whether the design of the decision environment, the choice architecture, or the market can affect the gender gap because they differentially activate a psychological attribute in which there are large gender differences. For example, when students decide about how much math to take in school, these choices are typically binding (once and for all choices) in continental Europe. In contrast, in the United States, education choices are much more flexible. American high school students, upon struggling in a difficult math class, may opt to take an easier one next semester. Choosing the difficult path of taking hard math courses is, therefore, a different choice in Europe than in the United States. This difference in the way decisions are made may in itself affect gender differences in choices of math-intensive courses. In his Fisher Schultz lecture, Roth (2002) has emphasized the role economists can play in designing markets as opposed to simply studying them. More recently, the investigation of the role of choice architectures on economic choices of agents is extensively reviewed and discussed by Thaler and Sunstein (2008). It may be time to expand the debate of choice architecture to understanding their impact on gender differences in choices.

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The study of gender differences in attributes as summarized in this chapter may change the way in which we interpret gender differences in labor market outcomes. We may start to attribute such differences not only to gender differences in abilities and discrimination, but to gender differences in preferences and attitudes. In addition, we should start investigating which policies may be successful in ensuring that gender differences in economic outcomes reflect underlying abilities. Market design could be expanded to include institutional and education design that helps women and men make choices that reflect their underlying preferences over outcomes rather than reflecting differences in attributes that play a role due to the environment in which these decisions are made.

II GENDER DIFFERENCES IN COMPETITIVENESS In this section I review the relatively new but very vibrant work on gender differences in attitudes toward competitions. Much of the work has been reviewed more extensively in an earlier survey by Niederle and Vesterlund (2011).6 The main motivation for the work on gender differences in competition is to shed light on possible reasons for gender differences in labor market outcomes, concerning vertical as well as horizontal segregation. Historically, the main explanations for these differences are differences in preferences over jobs, differences in ability, and discrimination (see references in Niederle and Vesterlund). In this chapter I review evidence of an additional explanation, namely, that there are gender differences in attitudes toward competition: women may be less likely to enter competitive and male-dominated fields and less likely to seek out promotions, and their performance may suffer in competitive environments compared to men. This research also provides a prime example of how experimental laboratory results interplay with work in the field. While gender differences in competitiveness have not been a topic of interest in the economics literature until the last decade, such differences have been documented in the educational and evolutionary psychology literature (Campbell 2002). Boys spend more time at competitive games than girls, while girls often select games that have no clear end point and no winner. These differences increase through puberty, and more men than women describe themselves as competitive. However, in contrast to most of the other work described in this chapter, there has been no earlier literature in social psychology studying gender differences in competitiveness (e.g., the Handbook of Social Psychology, fourth edition, Gilbert, Fiske and Lindzey (1998) does not have an entry on competition in the subject index). There are two methodological issues when studying gender differences in competitiveness. The first is that the experiments in this section differ from many “standard” economic experiments in that they use real-effort tasks. This has advantages and disadvantages. Real-effort tasks allow measuring actual performances of women and men under both competitive and noncompetitive incentive schemes. Furthermore, choices over incentive schemes indicate not only preferences over payment schemes, but also factors that are potentially important factors outside of the laboratory, such as beliefs about the ability to perform these tasks, for example. The disadvantage of a realeffort task is a loss of control as effort cannot be directly measured; only performance can be measured. Furthermore, the link between performance and effort is not always clear, for an early example see Jevons (1870). Some tasks may result in performance that is very inelastic in effort, and, as such, changes in incentive schemes may affect effort

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but not performance. In addition, Ariely et al. (2009) have shown that higher incentives can lead to lower performance, one explanation being that participants may choke when stakes are very high. Another disadvantage of a real-effort task is that because costs of effort cannot be measured easily, optimal choices are hard to compute. However, there are experimental techniques that minimize these disadvantages and allow researchers to draw sound inferences despite not knowing the costs of effort or the precise relationship between effort and performance. The second methodological issue is that experiments on gender differences in competitive attitudes may depend on the gender of the participant as well as the gender of the other subjects. The most common solution, and the solution employed in early experiments, is to physically show subjects against whom they are competing, which allows them to determine the gender of their competitors. The main reason for this approach is that directly mentioning gender could lead to priming or to experimenterdemand effects.7 I first describe laboratory experiments on gender differences in competition. I start with gender differences in preferences for competitive incentive schemes and discuss how this gap can be reduced. I then move to gender differences in performance under competitive incentive schemes, followed by a discussion of the field evidence of gender differences in competitiveness. The final part of this section concerns work that addresses the external relevance of gender differences in competition for education and labor market outcomes. II.A Do Women Shy Away from Competition? The first paper to address whether women and men differ in their choices of competitive incentive schemes is Niederle and Vesterlund (NV; 2007). Participants in the experiment choose between a noncompetitive piece-rate scheme and a competitive tournament incentive scheme. There are several possible explanations for why a woman and a man with the same chance to win the tournament may differ in their choices. For each of those, I present the design solution in NV. Explanation 1: Gender differences in attitudes toward competition. This will be the main hypothesis, so the experiment is designed such that other explanations can be ruled out. Explanation 2: Gender differences in beliefs about relative performance. Men enter the tournament more than women because they are more (over)confident. Psychologists and economists often find that men tend be more optimistic about their abilities than women. Design solution. Assess the participants’ beliefs about their relative performance in the competitive tournament scheme. Explanation 3: Gender differences in risk and feedback aversion. These are dimensions different from taste for competition that also impact the choice between a tournament and a piece rate incentive scheme. The tournament payment scheme not only is competitive, it is also more uncertain and provides more information about relative performance than the piece rate scheme. For both risk aversion as well as preferences over receiving feedback about relative performance, there may be gender differences. Design solution. Instead of directly controlling for risk and feedback aversion, participants make a decision between two incentives schemes which mimic both the

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uncertainty in payment and the provision of feedback without any actual competition taking place. Explanation 4: Gender differences in other regarding preferences. While a piece rate scheme has no externality on others’ payments, a competitive tournament generates both winners and losers. If there are gender differences in altruism, these may generate gender differences in choices. Design solution. The tournament is designed such that choosing the tournament is an isolated individual decision that has no externality and hence no payoff consequences on any other subject. In the experiment 2 women and 2 men were seated in rows to form groups of 4 participants. Participants knew they were grouped with other people in their row and could see each other, though NV never discussed gender during the experiment. Subjects perform a real effort task under various incentive schemes. The task is to add up sets of 5 two-digit numbers for 5 minutes, where the score is the number of correct answers. After each problem, participants learn the number of correct and wrong answers so far and whether the last answer was correct or not. Participants do not receive any feedback about relative performance (e.g., whether they won a tournament) until the end of the experiment. The experiment has four treatments, one of which was randomly chosen for payment at the end of the experiment. The first two treatments serve as a measurement of the subjects’ performance at the real effort task. Treatment 1—Piece Rate. Participants are given the 5-minute addition task under a piece rate pay of 50¢ per correct answer. Treatment 2—Tournament. Participants are given the 5-minute addition task, with the participant who solves the largest number of correct problems in the group receiving $2 per correct answer while the others receive no payment (in case of ties the winner is chosen randomly among the high scorers).8 Subjects do not receive any information about the performance of others; specifically, they are not told their relative rank in either the piece rate or the tournament or whether they won the treatment 2 tournament. Measuring performance in both competitive and noncompetitive environments serves to determine the money-maximizing incentive scheme for each participant. The average performances of the 40 women and 40 men under the piece-rate scheme were 10.2 and 10.7 problems, respectively. Under the tournament, women solved on average 11.8 problems, compared to the 12.1 of men. Neither of these differences was significant, although the performance in the tournament was significantly higher than under the piece rate for both women and men. This could be due to either increased effort in the tournament, which leads to increased performance, or because participants are learning how to better perform this task. The evidence points to learning.9 Of the 20 tournament groups, 11 were won by women and 9 by men. More importantly, women and men with the same performance in treatment 2 have the same probability of winning the tournament. This allows NV to use absolute performance rather than a computed chance of winning the tournament in their analyses of gender differences in tournament entry. In the third treatment, participants once again perform the 5-minute addition task but this time select, in advance, which of the two compensation schemes to apply to their performance—piece rate or tournament.

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Treatment 3—Choice. A participant who chooses piece rate receives 50¢ for each correctly solved problem. A participant who chooses the tournament has the treatment 3 performance compared to the treatment 2 tournament performance of the other participants in her or his group. If the participant has the highest performance, she or he receives $2 for each correct answer in treatment 3. Otherwise she or he receives no payment. Note that a participant’s choice in treatment 3 does not affect the payment on any other participant. This allows ruling out the possibility that women may shy away from competition because by winning the tournament they impose a negative externality. Further, the participant’s beliefs about others’ choices have no payoff consequences and, as such, should not influence choices. Finally, since the participant’s competitors were all required to perform in a tournament in treatment 2, the participant upon selecting the tournament in treatment 3 still has to outperform a tournament performance of her or his three competitors. Given the task 2 tournament performance, 30% of women and 30% of men have substantially higher earnings from a tournament payment.10 In fact, 35% of women and 73% of men enter the tournament (a significant difference). Figure 8.1a shows, for each tournament performance quartile of task 2, the proportion of participants who enter the tournament, for women and men separately. Regressions confirm that men have a significantly higher propensity to enter the tournament for any performance level.11 Tournament-entry decisions should be driven by beliefs about relative performance, not only the absolute performance of a participant. Therefore, just before the end of the experiment, after treatment 4, participants were asked to guess their performance rank among the 4 players in their group, both in the piece-rate and tournament treatments (treatments 1 and 2). Participants received $1 if their guessed rank corresponds to their actual performance rank. NV find that 30 out of 40 men (75%) believe that they were the highest performer in the treatment 2 tournament in their group of 4! Most of them were obviously wrong. Men are highly overconfident. Women are also overconfident as 17 out of 40 women (43%) believe they had the highest performance. However, men are significantly more overconfident than women given their actual rankings.

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Figure 8.1b shows the proportion of women and men who enter the tournament for each guessed tournament rank. The more confident a participant is, the more likely the participant is to enter the tournament. However, gender differences remain significant among those who guessed they had the highest or second-highest rank (both of which comprise the most common beliefs). A man with the same belief as a woman still has about a 30-percentage-point-higher chance of entering the tournament. Regressions show that controlling for performance, gender differences in beliefs account for roughly a third of the gender gap in tournament entry. To account for the effects of risk and feedback aversion on the decision to enter a tournament, NV assess the impact of those factors in treatment 4, which is as close as possible to treatment 3 while eliminating any tournament performance. Treatment 4—Choice of Compensation Scheme for Past Piece-Rate Performance. Participants decide between the piece-rate and tournament incentive schemes for their task 1 piece-rate performance, where a tournament choice results in a payment only if the participant had the highest treatment 1 piece rate performance in their group. There are gender differences in the propensity to prefer the piece-rate incentive scheme. However, the treatment 1 piece-rate performance and beliefs about their relative piece-rate performance, largely account for choices of women and men, with the remaining gender gap being economically small and not significant. Hence, in contrast to the situation where women and men decide whether to enter the tournament and then perform, eliminating any tournament performance—leaving only the impact of beliefs, risk, and feedback aversion—results in no gender gap. The results from treatment 4 suggest that gender differences in beliefs, feedback, and risk aversion do not generate a gender gap and hence cannot account for the gender gap in tournament entry in treatment 3. Finally, in a regression of treatment 3 tournament entry controlling for treatment 2 performance and beliefs about relative performance as well as controlling for the treatment 4 decision, significant gender differences in treatment 3 tournament entry remain. NV attribute this residual to gender differences in competitiveness. In terms of money maximizing choices, high-performing women enter the tournament too little and low-performing men too much. Note however, that the losses of a high-performing female not entering the tournament are substantial, while the losses of a low-performing male entering the tournament are lower since even in a piece-rate incentive scheme, their earnings would have been low. The result is that few women enter the competition and few women win the competition. II.B Replication and Robustness of Women Shying Away from Competition A series of papers presents treatments that introduce minor modifications to the original Niederle-Vesterlund design and find similar results—for example, Cason, Masters, and Sheremeta (2010), Healy and Pate (2011), Balafoutas and Sutter (2012), Balafoutas, Kerschbamer, and Sutter (2012), Dargnies (2012), Kamas and Preston (2012), Price (2012), Cadsby, Servátka, and Song (2013), Niederle, Segal, and Vesterlund (2013), Almås et al. (2014), Buser, Niederle, and Oosterbeek (2014), Dreber, von Essen, and Ranehill (2014), Lee, Niederle, and Kang (2014), Wozniak, Harbaugh, and Mayr (2014), and Sutter and Glätzle-Rützler (2015). There are two papers using the NV design whose results are not completely in line with NV. Müller and Schwieren (2012) do replicate that women enter tournaments less

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than men. Among participants who are expected to have higher monetary earnings from the tournament than from the piece-rate incentive scheme, women are 10 percentage points less likely to enter the tournament; however, this difference is not significant. A sole failure to reproduce the basic gender gap of NV is provided by Price (2010), who fails to find gender differences in preference for competition. Furthermore, despite the use of very different designs, a series of other papers, some of which are discussed in more detail later, also identify circumstances in which women, conditional on performance, enter tournaments less often than men—for example, Gneezy, Leonard, and List (2009), Kamas and Preston (2009), Vandegrift and Yavas (2009), Ertac and Szentes (2010), Dohmen and Falk (2011), Booth and Nolen (2012), Cárdenas et al. (2012), Kamas and Preston (2012), Mayr et al. (2012), Shurchkov (2012), Gupta, Poulsen, and Villeval (2013), and Andersen et al. (2013). The existence of a gender gap in tournament entry has stood the test of replication. I next describe the extent to which the limited impact of gender differences in other traits, such as beliefs, risk aversion or other regarding preferences hold up. BELIEFS NV directly elicited beliefs on relative ability and used them as controls in the tournament-entry decision. Papers using this approach typically show that men are more confident than women, that beliefs help explain the gender gap in winner-takeall tournament entry, and that a significant gender difference remains when controlling for beliefs—for example, Grosse and Riener (2010), Healy and Pate (2011), Balafoutas, Kerschbamer, and Sutter (2012), Balafoutas and Sutter (2012), Dargnies (2012), Shurchkov (2012), Kamas and Preston (2012), Niederle, Segal, and Vesterlund (2013), Almås et al. (2014), Buser, Niederle, and Oosterbeek (2014), Wozniak, Harbaugh, and Mayr (2014), and Sutter and Glätzle-Rützler (2015). A few papers find that gender differences in beliefs can account for the gender gap in tournament entry. These are Kamas and Preston (2009), who examine a ranked-order tournament in which each rank receives a different piece rate, Cadsby, Servátka, and Song (2013), and Dreber, von Essen, and Ranehill (2014). An alternative to directly measuring beliefs as in NV and related studies is to change beliefs by providing participants with information about their relative performance. There are three studies that assess the impact of such information on tournament entry. In all of them, information affects tournament entry. In Cason, Masters, and Sheremeta (2010), a significant gender gap remains, while in Ertac and Szentes (2010) and Wozniak, Harbaugh, and Mayr (2014), information on relative performance eliminates the gender gap in tournament entry, though for Wozniak et al., a significant gender gap in tournament entry remains among participants who are expected to have higher earnings from the tournament. RISK ATTITUDES To assess the role of risk attitudes, NV employed two strategies. First, treatment 4 mimicked the treatment 3 tournament choice as much as possible while eliminating any tournament performance and second, they used decisions in treatment 4 as a control when estimating gender differences in the treatment 3 tournament-entry decision. The same approach has been used by Dargnies (2012), Healy and Pate (2011), and Niederle, Segal, and Vesterlund (2013), who replicate NV’s result that risk has only a minor impact on gender differences in tournament entry.12

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Other approaches confirm the minor role of risk attitudes in accounting for gender differences in tournament entry. Grosse and Riener (2010) have participants choose an incentive scheme for a number to be randomly drawn, rather than a real performance. Cadsby, Servátka and Song (2013) have subjects choose between a piece rate and chance pay. In chance pay, the subject has a 25% chance to receive the tournament payment per each correct problem (which equals four times the piece-rate payment) and otherwise receives no payment. They found no significant gender differences in choosing the chance pay over a piece rate.13 A more common approach in the recent literature has been to directly elicit risk attitudes through a series of incentivized lottery choices and use those as controls. The common finding is that the risk measure has no large impact on the gender gap in tournament entry; see Cason, Masters, and Sheremeta (2010), Kamas and Preston (2012), Almås et al. (2014), Buser, Niederle, and Oosterbeek (2014), Wozniak, Harbaugh, and Mayr (2014), and Sutter and Glätzle-Rützler (2015).14 OTHER-REGARDING PREFERENCES While in a naïve design gender differences in altruism could impact gender differences in tournament entry, the experiment in NV was specifically designed in such a way that concerns for altruism play no role. This is because, by design, a subject’s decision whether to enter the treatment 3 tournament had no payoff externalities on any other subject. Nonetheless, it could be that specific other-regarding preferences correlate with a preference for competitiveness and account for the gender gap in those preferences. The treatment 4 choice of NV mimicked the treatment 3 tournament-entry choice in all aspects, including the role of other-regarding preferences but excluding any tournament performance. Using the treatment 4 choice, NV found no evidence that other-regarding preferences could account for the gender gap in tournament entry. Several papers use various measures of other-regarding preferences and in general replicate that such measures do not play a large role in accounting for the gender gap in tournament entry; see Teyssier (2008), Kamas and Preston (2009), Bartling et al. (2009), Dohmen and Falk (2011), and Almås et al. (2014). Only Balafoutas, Kerschbamer, and Sutter (2012) found that controlling for beliefs, risk, and distributional preferences eliminates the gender gap in tournament entry. THE ROLE OF THE TASK NV selected a 5-minute addition task because it requires both skill and effort and because research suggests that there are no gender differences in ability on easy math tests.15 However, participants could perceive the task as a stereotypical male task. Changing the task to a neutral or stereotypical female task could affect the gender gap in tournament entry through many ways. It could change the gender gap in beliefs about relative performance, affect the extent to which women and men care to receive information about their relative performance, or simply affect the benefits (or costs) from performing in and winning the tournament. While most papers use the NV math task, they all use a different word task, ranging from forming words using letters out of an 8-letter word to ordering 5 words in a sequence so they form a sentence. Almost all papers found gender differences in tournament entry in the math but not the verbal task; see Kamas and Preston (2009), Grosse and Riener (2010), Shurchkov (2012), and Dreber, von Essen, and Ranehill (2014). Only Wozniak, Harbaugh, and Mayr (2014) find gender differences

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in tournament entry both in a math and a verbal task, controlling for performance and beliefs; in fact, in their paper the task has no significant impact on tournament entry. In summary, the existence of a gender gap in tournament entry in stereotypical male tasks persists after controlling for actual performance, beliefs about the relative performance, risk attitudes, and other-regarding preferences. The treatments that consistently reduce and at times eliminate the gender gap in tournament entry is providing information on relative performance or changing the task to one in which women are believed to have an advantage. II.C Reducing the Gender Gap in Tournament Entry The fact that high-performing women do not enter competitions and hence don’t win is disconcerting, not only for those women but perhaps also from a societal point of view. How can this gender gap in competitiveness be reduced? There are two major avenues of research to address this. The first could loosely be described as trying to understand what factors, such as hormones, age, socioeconomic status, culture, and so on, generate the gender gap in competitiveness. This line of work can help understand whether it may be possible to “fix the competitiveness of women” or whether gender differences in competitiveness are immutable. The second approach can be loosely described as “fixing the institutions.” This consists of work that studies what institutions might be the most prone to enhance or reduce the impact of gender differences in competitiveness. II.C.I WHAT FACTORS GENERATE THE GENDER GAP? Hormones and MRI studies. Results on this dimension are quite mixed. Buser (2012) finds that women (in single-sex groups) are less likely to enter competitions during the phase of the menstrual cycle when the secretion of progesterone and estrogen is particularly high. Wozniak, Harbaugh and Mayr (2014) considering mixed-sex tournaments find just the opposite. Whereas Apicella et al. (2011) find no relationship between self-selection into a tournament and current testosterone levels, Hoffman and Gneezy (2010) take advantage of the fact that left-handedness is thought to be an indicator of prenatal testosterone and find that left-handedness increases competitiveness. Another possible basis for gender differences in competitiveness is the possibility that men’s and women’s brains are wired in such a way that their brains react differently to differences in relative income. Dohmen et al. (2011) investigate this, finding that activities in brain areas related to rewards react positively to higher absolute income and negatively to lower relative income. However, they did not find any gender differences in this respect. Clearly no obvious consensus has been reached in understanding which biological differences between women and men can directly impact the gender gap in competitiveness. Age. One problem in assessing how competitiveness changes with age is that participants at different ages will have had different life experiences that could affect competitiveness. For example, young employees at a firm may have diverse competitive backgrounds, though older employees may perhaps be more competitive (if they have been promoted in the company) or less competitive (if they still have not received a superior position). There are also potential selection effects in terms of who signs up for the experiment; for example, visitors to a specific locale such as a mall may comprise

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young males who are less competitive than average (since the others work) and older people of average competitiveness (since they are all retired). Both problems can be avoided by having representative population samples or having participants who are expected to be in the same environment for a wide range of ages, such as, for example, children at a typical K–12 school. Looking at children, Sutter and Glätzle-Rützler (2015) examine compensation choices of 1,000 Austrian children and teenagers ages 3 to 18. Using a math task for the older participants and a running task for the younger subjects, they find a persistent gender gap in tournament entry. Despite there being no gender gap in performance on either of these tasks, boys, independent of age, are 20 percentage points more likely to enter the competition than girls. Thus the gender gap in competitiveness is already present by age three. Several papers consider subjects older than undergraduates. Mayr et al. (2012) recruit around 500 people in an indoor shopping mall who perform in an NV-style design with pairwise competition. They find that 56% of men but only 36% of women choose to compete, a difference that remains relatively stable across age (see Figure 8.2). They find that beliefs regarding relative performance ranking (they ask for percentiles) do not vary with age and account for only a small fraction of the gender gap in tournament entry. Leibbrandt, Gneezy, and List (2013) study villagers from a region in Brazil who either fish individually (they live close to the lake) or collectively (they live close to the sea). They find that the more experienced (or older) fishermen are, the more competitive they become in the individualistic society compared to those who live in the cooperative society. Women who live (but don’t fish) in the individualistic or competitive society do not differ in their choice of tournament versus piecework pay, so overall they look more like men in the collectivist society. This suggests that the gender gap in tournament entry depends on past experience and either grows over time for men who work individually or remains constant (and perhaps shrinks a little) for men working in groups.

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Charness and Villeval (2009) have two subjects decide between a piece rate and a tournament pay for an anagram task, where the person who chooses the tournament wins by default if the other chooses the piece rate. In this case choice depends not only on beliefs regarding performance, but also on beliefs about others’ choices, with the latter beliefs not elicited. Contrary to NV’s results, they find no gender difference in tournament entry. They also find no impact of age when conditioning on beliefs about relative performance. The exception to the latter is that retirees enter a little less than undergraduates. The effects of age and work experience on competitiveness and its effect on the gender gap in competitiveness are clearly not completely resolved. However, it seems that in the Western world, gender differences in competitiveness are already present among children. Socio-Economic Status. Almås et al. (2014, 1) consider Norwegian ninth graders and find that “children from low socioeconomic (SES) status are much less willing to compete than children from medium or high SES families, and this result holds when controlling for confidence, performance, risk- and time preferences, social preferences, and psychological traits. Second, family background is crucial for understanding the gender difference in competition preferences. . . . [G]irls from well-off families are much less willing to compete than boys from well-off families, while we do not find a statistically significant gender difference in competitiveness preferences among children from low socioeconomic status.” They find that this difference in the gender gap in tournament entry conditional on SES is driven by boys with a low-SES father, as they are much less willing to compete than other boys. Bartling, Fehr, and Schunk (2012) have 4- through 7-year-old German children decide between a piece rate and a tournament pay, where each child knows they will compete against another randomly chosen child of the same sex and age. As expected (see Section II.C.2, where I summarize the literature showing that the gender gap in tournament entry is much reduced when women compete against other women), the paper finds no gender differences in choice of compensation scheme in these single sex tournaments. However, for children from low socioeconomic background, bad health implies less competitiveness. Furthermore, children who have more siblings, as well as those earlier in the birth order, are more likely to compete. Big Five Personality Characteristics. Apart from hormonal differences and differences in risk preferences and confidence, researchers have tried to assess whether other personality traits can account for the gender gap in competitiveness. Most prominently among these personality characteristics are the Big Five, which are openness to experience, conscientiousness, agreeableness, extroversion, and neuroticism. This reflects a growing interest among economists to understand the impact of the Big Five on labor market outcomes, see, for example, Borghans et al. (2008). Müller and Schwieren (2012) correlate an NV-style measure of competitiveness with the Big Five. They find that neuroticism significantly negatively correlates with tournament entry, a trait in which women score higher. They then show that controlling for neuroticism reduces the gender gap in tournament entry. Almås et al. (2014) do not find that any of the Big Five have a significant impact on tournament entry, nor does controlling for any of the Big Five traits reduce the gender gap in tournament entry. Clearly, this line of research is just beginning.

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Priming. Cadsby, Servátka and Song (2013) prime subjects concerning either gender/family or professional issues. Priming was administered through a questionnaire at the very beginning of the experiment. Gender or family-related concerns include questions such as, What is your gender? and Do you have children? while professional concerns are questions such as, What is your GMAT score? and What is your salary expectation upon the completion of your degree?16 They find that priming for professionalism significantly reduces the gender gap in tournament entry, whereas professional priming positively impacts women with respect to both their beliefs and their preference for tournament incentives. Culture. A few papers have studied the impact of cultural differences on the gender gap in competitiveness. Gneezy, Leonard, and List (2009) compare the choice of a tournament-incentive scheme for patriarchal Maasai in Tanzania and the matrilineal Khasi in India. They find that among Maasai, behavior corresponds to that of the Western world: men are more likely to opt for a tournament incentive scheme than women. However, the gender gap reverses among the Khasi, where women are more competitive. Their design does not assess the impact of beliefs on these differences. Cárdenas et al. (2012) find a gender gap in tournament entry among Swedish children 9–12 years old, but not among Columbian children. “We used a similar scale to elicit how important the children consider competing against a boy and against a girl to be (0 = not at all important, 10 = very important). In both countries, boys rate competition as more important compared to girls (Colombia: p = 0.009, Sweden: p < 0.001). In Colombia, both girls and boys believe that it is more important to compete against a boy than against a girl (Girls: p = 0.003, Boys: p < 0.001). Girls in Sweden rate competing against a boy as being more important compared to competing against a girl ( p < 0.001), whereas boys rate it as equally important ( p = 0.347)” (p. 21). II.C.2 FIXING INSTITUTIONS TO REDUCE THE GENDER GAP In addition to asking what makes men and women differ in their competitiveness, we can explore the role of institutions under which competition takes place. One possible way would be to provide participants, especially women, with feedback about their chances of winning the tournament. While this is easy to implement in the laboratory, outside the lab, such information on relative tournament performance may be hard to come by. Another prominent institutional change is to make competitions more gender specific, either through single-sex competitions or a quota-style affirmative action. Affirmative Action. Niederle, Segal, and Vesterlund (2013) study whether a form of explicit affirmative action, namely, a “soft” quota, which basically makes the competition more gender specific, can increase the number of high-performing women that enter a tournament. The setup is like in NV, using the same task, though now with groups of 3 men and 3 women (and mentioning the gender composition of the group explicitly). The first 3 treatments are just like in NV, only in the tournament the 2 highest-performing participants receive compensation equal to 3 times the piece rate per correct answer (where 2 out of 6 win the tournament).17 After the first 3 treatments (piece rate only, tournament only, and the Choice treatment, an Affirmative Action Tournament is introduced, in which the 2 winners are chosen as follows. One winner is the highestperforming woman; the second winner is the person with the highest performance in the remainder of the group. That is, a woman wins the tournament if either she is the

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highest-performing woman or if she has 1 of the 2 highest performances. A man only wins if he is both the highest-performing man and among the top 2 performers overall. While in this experiment gender was mentioned and men outperform women, the results in terms of gender differences in the decision to enter a tournament mimic those of NV almost exactly. Once affirmative action is introduced, women enter the affirmative-action tournament at a much greater rate (both relative to the standard tournament and relative to payoff maximizing choices), while men drop out at a higher rate than predicted. Niederle, Segal, and Vesterlund show that several channels are responsible for the change in the gender gap in tournament entry. First, there is an effect of purely mentioning affirmative action; women increase their tournament entry, though the effect on men is small. Second, the gender gap in beliefs vanishes when beliefs are about relative performance within gender rather than in mixed-gender groups. However, even controlling for both those effects, women are more likely to enter the competition when they just have to outperform other women compared to when they compete against a mixed-gender group. It seems that the gender-specific competition alters the pleasure or fear of competition or attitudes toward competition in general. To assess the effect of affirmative action, note that the number of tournament entrants at or above a specific threshold level is almost always either the same or higher under affirmative action than under the standard tournament. The implications for this are as follows: Assume affirmative action was not announced but used “secretly,” after subjects decided whether to enter the tournament. Consider the rule to hire at least one woman for every man and being able to hire only among those participants who entered the tournament. Such an affirmative action rule would be very costly, in the following sense. When hiring participants, in order to assure having at least one woman for every man, at some early point the woman hired to fulfill the quota would be much worse than the best unemployed man. That is, many qualified men will be passed by to hire a woman. On the other hand, when affirmative action is announced, the pool of entrants to the affirmative action tournament is such that for almost all performance thresholds, there are as many women as men who perform at that threshold or higher. That is, in order to hire a woman to fulfill the affirmative action requirement, the men that are passed by are “only” of the same, but not of a higher, performance level than the woman is. In that sense, affirmative action is not costly and is definitely much less costly when it is announced in advance and when women have a chance to adjust their tournament entry decisions accordingly than when it is implemented secretly. To summarize, in an environment without discrimination, but in which the playing field is not level in that there is a gender gap in tournament entry, a quotalike affirmativeaction setting in which women have to compete only against other women can reduce the gender gap in tournament entry and, in particular, increase the fraction of highperforming women who enter a tournament. This experiment and the results have been replicated (though published earlier) by Balafoutas and Sutter (2012), who in addition consider another affirmative action device, namely, preferential treatments in which the performance of women is increased by one or two problems, respectively. Those also reduce the gender gap in tournament entry. Several papers consider single sex tournaments, and contrast the results with those obtained in mixed-sex tournaments. In Sutter and Glätzle-Rützler (2015), Austrian children ages 9 through 18 choose whether to enter a tournament in an NV design, when either in a group of 2 boys and 2 girls or in a single sex group of 4 children. They do not

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find that the gender composition of the group affects choices. Likewise, Gupta, Poulsen, and Villeval (2013) consider pairwise competition, where each participant receives an assigned first name that corresponds to their gender, which can be observed by their opponent. If only one subject chooses the tournament, that subject wins with certainty. Otherwise, the subject with the highest performance wins. The main result is that men enter the tournament more than women. Furthermore, everyone believes that men are more likely to enter the tournament. Oddly enough, choices of tournament entry do not depend on the gender of the opponent. In contrast, Booth and Nolen (2012) consider children just under 15 and find that girls in single-sex groups (of 4) enter the tournament more than girls who face at least 1 boy. Girls are not affected by how many boys they face, conditional on facing at least 1, and boys do not care about the gender of their competitors. Finally, several researchers gave participants the option to choose the gender of their competitor. In a math task; both Gupta, Poulsen, and Villeval (2013) and Grosse and Riener (2010) find that men and women prefer to compete against women. In addition, Grosse and Riener find that for a verbal task, half the participants prefer to compete against women and half, against men. In summary, the majority of the evidence to date indicates that single-sex tournaments, or quotalike affirmative-action tournaments, reduce the gender gap in tournament entry without seriously diluting the quality of the resulting entrants. Given that some papers do not find that these alternative tournament structures increase entry, more work is needed to confirm that the positive effect of single-sex competitions is robust. II.D Performance in Tournaments The decision to enter a tournament is not the same as the decision (or ability) to provide high effort once in a tournament. The literature discussed so far studied the decision whether to enter a tournament, which we could think of as the extensive margin, where large gender differences were found. The first economic experiment on gender differences in competitive attitudes tested for gender differences on the intensive margin—that is, whether women and men react differently when forced to perform in a competitive environment. To test for gender differences in performance once in a tournament, it is crucial to find a real-effort task in which performance is not only statistically but economically significantly affected by the incentive scheme and, hence, presumably, by effort.18 Gneezy, Niederle, and Rustichini (GNR; 2003) conduct an experiment at the Technion in Israel, a high-profile technical university. Women and men solve mazes on the Internet for 15 minutes under various incentive schemes. In each session (apart from single-sex sessions) there were always exactly 3 female and 3 male participants. They could see each other and determine the gender composition of the group, though no mention of gender was explicitly made. Each treatment had 30 women and 30 men, where no one participated more than once. At the end of the experiment participants are informed only of their own earnings. Piece-Rate Treatment. In the piece-rate treatment participants receive about $0.50 per completed maze. Subjects have 15 minutes to solve as many mazes as they can on the Internet. The task is the same for all treatments. The average performance in the piece-rate treatment for men is 11.23 mazes, while it is 9.73 for women. The difference of 1.5 mazes is not statistically significant.

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Tournament Treatment. In the tournament treatment, only the highest-performing participant of the 3 men and 3 women receives a payment for each solved maze, which equals 6 times the piece-rate payment, $3 per maze. In case of a tie, the winners share the payment equally. The average performance of men is 15, which is significantly higher than in the piece rate. The average performance of women is 10.8, not significantly different from the piece-rate performance. The gender gap in tournament performance of 4.2 is significant. Most importantly, the gender gap in tournament performance of 4.2 is significantly higher than the gap of 1.5 in the piece-rate performance. The significant increase in the gender gap in mean performance when moving from a piece rate to a tournament scheme could be the result of two changes. First, the payment scheme became more competitive. However, the tournament payment is also more uncertain, compared to a piece-rate scheme. And indeed, there is a large literature on possible gender differences in risk aversion (see Section V). One option for assessing the potential impact of (possible) gender differences of risk aversion on changes in performance as the incentive scheme becomes more competitive is to elicit risk attitudes of women and men. One problem with this indirect approach is that the magnitudes of gender differences on risk aversion could depend on the specifics of the environment used to measure them. Because the object of interest is a real-effort task, it is not clear what the relevant range of lotteries should look like, since for example, costs of effort to solve mazes cannot be easily assessed. It may prove even more difficult to extrapolate to effort choices under tournament incentives because it could be that there is additional aversion when there is uncertainty about the relevant lotteries in play, as participants may not be clear about the risk they are facing or, alternatively, the chances of winning the tournament for a given effort level. Instead, GNR opt for a direct approach to assess whether women and men react differently to uncertainty in payments that are inherent in tournaments. Subjects have to perform in a random-pay treatment, which is similar in terms of uncertainty to the competitive-pay treatment, though without any competitive aspect. Random-Pay Treatment. Only 1 participant of 6 receives compensation equal to the tournament payment, 6 times the piece-rate scheme, that is, $3 per maze. However, the person who receives payment—the “winner”—is chosen randomly, as opposed to depending on the number of mazes solved as in the tournament. The average performance of women and men is just like in the piece-rate treatment. Furthermore, differences in performance between the random-pay and the tournament treatment are just like those between the piece-rate and the tournament treatment. GNR conclude that the significant change in the gender gap in mean performance when moving from the piece rate to the tournament can indeed be attributed to changes in the competitiveness of the incentive scheme and not to changes in the uncertainty of payment inherent to participating in a tournament. There remain four classes of explanations for increased performance of men versus women conditional on performing in a tournament: First, it could be that women cannot solve more mazes without incurring very high costs.19 Second, it could be that women simply do not perform well under competition (in general), because they do not like to, or cannot, compete. Third, it could be that women can compete well, but not against men. This could be because women perform somewhat less well in this task than men, and hence they may decide not to increase their performance by not increasing their effort. In addition, this could be driven by women’s beliefs that they perform less well than men.20 Finally, the performance that needs explaining is perhaps not that of women,

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but that of men. It could be that men compete too much. This could be because men receive a direct utility boost from winning a tournament or because men really like to compete and win, and perhaps this is especially the case when there are women around. To assess the validity of each of those hypotheses, GNR run a treatment where 6 participants compete in single-sex tournaments. Single-Sex Tournament Treatment. In the single-sex tournament, treatment groups comprise either 6 men or 6 women. The incentives are just like in the tournament treatment, that is, the highest performer, the winner, receives 6 times the piece rate payment per maze, and everyone else receives no payment. The performance of men (average of 14.3) is not significantly different from those in mixed tournaments and is significantly higher than in piece rate and random pay. That is, it does not appear that men compete only when they’re competing against women. More importantly, women do seem to react positively to competitive incentive schemes in the single-sex environment. Their performance in the single-sex tournament (on average 12.6) is significantly higher than in either the piece-rate or the random-pay treatment. To assess whether women respond to competitive incentive schemes in single-sex groups as much as men do, GNR compare the average gender differences in performance across treatments. The gender gap in performance is 1.5 in both the piece-rate and the random-pay treatment and is 1.7 in the single-sex tournament. However, the gender gap in mean performance is 4.2 in mixed tournaments, significantly higher than in the single-sex tournaments ( p = 0.08), and in all other treatments (see Figure 8.3a).21 This suggests that the third explanation is the most likely: women can compete well, just not when they have to compete against men. Figure 8.3a shows that there is a significantly larger gender gap in mixed competitive environments compared to both noncompetitive payment schemes and a single-sex competitive environment. To describe how average experience from Figure 8.3a translates into individual behavior, Figure 8.3b shows, for each decile, the proportion of women above that performance decile, starting from the top 10%. The figure shows, for example, that the fraction of women among the top 40% of performers varies a lot. In the noncompetitive

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treatments and in the single-sex tournament, among the top 40% of performers, about 60% of them are male and about 40% are female. The fraction of women among the top performers for any decile is basically the same, whether single-sex tournaments or noncompetitive treatments are used. Hence, if tournaments were run in singlesex groups, one may falsely conclude that men and women have similar responses to competition. However, running mixed-sex tournaments significantly decreases the fraction of women with a performance in the top 40%, from about 40% to 24%. Women are less represented among top performers in mixed tournaments compared to any other incentive scheme when considering any performance above any specific decile but the very highest. Thus mixed-sex competitions result in a decrease in the fraction of women among top performers. There are several papers that investigate whether gender differences in performance are exacerbated in mixed-sex competitions under a variety of conditions. The first of these is Gneezy and Rustichini (2004). They consider performances of 10-year-olds in competitive and noncompetitive environments. Children first run 40 meters separately and then are matched up so that the 2 fastest children run against each other, and so on. They find no initial gender difference in speed. In competition, boys increase speed on average, while girls become slightly slower, a difference that is significant. Furthermore, a second group of children who run a second time in a noncompetitive way show no significant gender difference in speed. This suggests that boys and girls did not simply become differentially tired the second time, but rather seem differentially affected by the competition. Both boys and girls improve the most when competing in mixed groups, boys competing against boys also run faster, but girls competing against girls slow down somewhat. That is, with respect to running speed, boys improve more than girls when moving from noncompetitive performances to a competition. However, results on running speed fail to replicate that girls compete more against female opponents than male opponents. One thing to note from this study is that children physically ran against each other; in this setting one feedback is very salient—the winner of the race is easily determined. Therefore, one variable of interest is not how fast boys and girls were, but whether they won the competition. The initially faster child wins the competition 10 out of 17 times (59%) in male groups and 6 out of 12 times (50%) in female groups. That is, the initially faster runner is equally successful at winning in homogenous groups compared to the initially slower child. In contrast, in mixed groups, 8 out of 11 times the boy won when he was initially slower (73%) and 15 out of 18 times (83%) when he was initially faster. Viewed this way, the results suggest that girls do not compete well against boys. Girls have a higher chance of winning whenever running against another girl than against a boy, independent of whether they were initially faster or slower. On the other hand, a boy has an easier time winning against a girl than another boy, irrespective of whether he was initially slower or faster. In summary, running speed replicates that boys improve their performance more than girls when moving from a noncompetitive to a competitive environment. This is replicated when considering who wins the competition. In addition, a specific girl has a higher chance of winning the competition if she competes against another girl rather than a boy. Several subsequent papers have employed an approach similar to Gneezy and Rustichini (2004). Cotton, McIntyre, and Price (2013) have American third, fourth, and sixth graders repeatedly perform in pairwise competition against a known, though in each case against a different, classmate. Using a math task, they find a gender gap in

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performance in the first, but not in subsequent tournaments. This is driven by lowability males initially overperforming and high-ability females initially underperforming compared to later rounds. Cárdenas et al. (2012) have 9- to 12-year-old children first perform under a piecerate scheme, then an assortatively matched (by piece-rate performance) pairwise tournament. They find no significant increases in the gender gap in performance among Columbian children, and in 2 out of 4 tasks Swedish girls actually increase their performance in competition more than boys do (in rope jumping, where girls are already much better in the piece rate, and in math, where girls increase their performance but remain worse than boys who don’t change their performance). There are no controls as in Gneezy and Rustichini (2004) to assess the effects of learning or fatigue on the observed changes in performance. Considering designs closer to GNR, Günther et al. (2010) and Shurchkov (2012) consider stereotypical male tasks—mazes and a math task, respectively. Both papers find that while men and women perform equally under a piece-rate scheme, men outperform women in the tournament. On the other hand, Freeman and Gelber (2010) have participants solve mazes in groups of six, randomly formed among participants, first under a piece rate and then under various tournament schemes. While they find that participants solve more mazes in round 2 and do so differently depending on the exact round 2 payment scheme, they find no significant gender difference in round 2, given round 1 performance. Bracha and Fershtman (2013) have participants allocate time within 10 minutes between a mindless filing task—deciding whether a number is odd or even—and a more challenging sequence task, where subjects are given 3 numbers and have to fill in the missing fourth number. They find that performances of women and men are not affected by the payment scheme, piece rate or tournament, and neither is the gender gap in performance. Finally, Dato and Nieken (2014) consider pairwise competition where participants, in addition to deciding how hard to work, can also decide to sabotage the opponent. They find that men sabotage more and hence win more often, but, because sabotage is costly, don’t have higher earnings. In a treatment that controls for the gender of the opponent, they show that both men and women believe men sabotage more, though gender differences in beliefs about others’ sabotage propensity cannot fully account for the gender gap in sabotage.

II.D.1 EFFECT OF DIFFERENT TASKS Günther et al. (2010) and Shurchkov (2012) consider a stereotypical male task— mazes and a math task, respectively—and a stereotypical female task, a word task— forming words that start with a specific letter and forming words out of a given set of letters, respectively. Both papers find that for the stereotypical male task, men outperform women in the tournament but perform equally under a piece-rate scheme. No such gender effects are found in the verbal task. Shurchkov also considers a “low-pressure” environment, where each task lasts 10 instead of 2 minutes, and finds that there is no significant gender gap in the math task, though women perform higher than men in the verbal task. More recently, Cotton, McIntyre, and Price (2013) find a gender gap in a first tournament performance for a math, but not for a verbal, task.

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II.D.2 THE ROLE OF BELIEFS To assess the role of beliefs and feedback on gender differences in performance, Kuhnen and Tymula (2012) have participants perform in 18 rounds in which, before each performance, participants learn whether they will receive information about their relative performance with a 0%, 50%, or 100% chance. The feedback provides information on one’s ranking and the scores of all group members. Participants have no other incentives to perform. The authors find that participants have a higher performance when there is a positive chance to receive feedback; that is, it appears that solely providing relative performance feedback may activate competitive attitudes. Furthermore, the number of men in the group affects the productivity of women. The women’s expected and actual rankings are worse and their absolute performance is lower when there are more men in the groups. Men, however, are not affected by the gender composition of the group. Thus, the results mirror those of GNR if performance under the threat of feedback is akin to a competition. II.D.3 SUMMARY Gender differences in performance increase when moving from a competitive to a noncompetitive incentive scheme, a result that has been replicated several times. This implies that a woman with ability and performance in a noncompetitive piece-rate scheme comparable to that of a man will have an inferior performance to that man if the performance is measured in a competitive environment where women and men compete against each other. Put differently, performances under mixed-gender competitions may not equally reflect underlying abilities of women and men. To obtain this result, it is crucial to consider tasks in which performances change when participants perform under a piece-rate scheme or a tournament scheme, presumable because they work harder under the tournament. For example, the task in NV of adding up five two-digit numbers for 5 minutes does not fulfill this requirement. Occasionally no changes in the gender gap in performance have been observed, and in one paper, Cárdenas et al. (2012), females actually increase their performance more than males on one of the tasks as the incentive scheme became more competitive. Just as in the literature on tournament entry, more research is needed to assess the extent to which differences in task characteristics can help account for variations in the change in the gender gap in performance when moving from a noncompetitive to a competitive environment. Finally, there is some evidence that in cases in which mixedsex competitions harm the relative performance of women compared to noncompetitive treatments, women are as competitive as men, as long as they don’t have to compete against men.22 This would imply that affirmative action in the form of quotas may result in performances of women that are more in line with their underlying ability and comparable to that of men. Once more, this finding is still to be considered a hypothesis rather than a firmly established result. II.D.4 LINKING TOURNAMENT ENTRY AND PERFORMANCE IN TOURNAMENTS We can draw a parallel between gender differences in choice of incentive schemes and gender differences in performance across incentive schemes, exemplified in the papers by Niederle and Vesterlund (2007) and Gneezy, Niederle, and Rustichini (2003). In GNR, let “compete” mean to perform highly in a competitive environment and in NV, to enter a competitive environment. Then both papers show women do not

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compete against men. GNR also analyzed single-sex tournaments and found that women compete against other women just fine. The corresponding result has been found in the literature on tournament entry, with research showing that women who do not enter tournaments against men do, in many cases, enter tournaments where they have to compete only against women. Note that NV aimed to rule out the effects of GNR by using a task in which performance was not affected by the incentive scheme. Future research should provide a link between the two approaches and assess whether women whose performance in a competition does not reflect their piece-rate performance tend to shy away from competition. Together, the results following NV and GNR show that women are less competitive than men. The last decade saw lots of work in the experimental literature on gender differences in competitiveness. Recently, this literature has also found its way into field evidence as well as field experiments. II.E Field Experiments on Gender Differences in Competitiveness Much of the field evidence consists of data that had no variation imposed by an experiment. I refer the interested reader to Niederle and Vesterlund (2011) for an overview of this literature. I will detail only two such field studies to provide a flavor of the existing results and then survey field experiments on gender differences in competitiveness. Ors, Palomino, and Peyrache (2013) consider performance in a competitive entry exam to a very selective French business school (HEC), where slightly more than 10% of applicants are accepted each year. Men perform significantly better than women at this admission contest. A couple of years earlier, those same applicants took the very stressful, but noncompetitive (i.e., graded on absolute performance) high school exam. In the high school exam, female HEC applicants performed significantly better than male HEC applicants. Similarly, for students who were admitted and accepted to HEC (a selected sample), women performed better than men in the first year of the program, though only in the nonmathematics-oriented classes. In both of these cases performance, while measured under a stressful environment, is graded more on an absolute level and not solely on a relative level. The fact that women perform worse than men only under the competitive entry exam suggests that competitive exam scores reflect skills as well as responses to competition. The findings therefore corroborate the experimental results of an increased gender gap in performance when performance is measured under a competitive rather than a noncompetitive incentive scheme. Morin (2015) studies grades at the University of Toronto and exploits the fact that an educational reform resulted in a “double cohort,” since in one year two cohorts, namely previous twelfth (the new final high school year) and thirteenth (the previous final high school year) graders competed for university grades, which are based on a curve. He finds that the gender gap in grades, controlling for background such as preuniversity grades, significantly increased in the year of the double cohort, the year in which there was fiercer competition. This gender gap generated by increased competition is present at all performance levels. In a field experiment, Lavy (2013) considers teachers who are paid cash bonuses based on improvements in the test scores in their class, where payment depended on relative improvements within a specific field and school. This resulted in a variation in the gender composition of competitors. Lavy does not find gender differences in

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improvement, nor does he find that the gender composition of the group of competing teachers influences outcomes. Delfgaauw (2013) considers team competitions and finds that sales competitions have a large effect on sales growth, but only in stores where the store’s manager and a sufficiently large fraction of the employees have the same gender. More recently, Flory, Leibbrandt, and List (2010) conduct a field experiment on gender differences in tournament entry. They randomly offered job seekers compensation schemes that varied in the degree of competition. They find that women are relatively less likely to apply for a job with a competitive payment scheme than men. II.F External Relevance of Competitiveness It is comforting that gender differences in competitiveness can be replicated using samples other than undergraduate students and using tasks that last longer than several minutes. However, the (experimental) field evidence, in general, cannot directly assess the external relevance of competitiveness, that is, the role of gender differences in competitiveness in accounting for gender differences in education or labor market outcomes. There are two reasons for that. First, any experimental evidence, be it in the laboratory or the field, cannot experiment with education and work decisions on a scale that mirrors those of a general population. For example, field evidence on Austrian farmers, assessing their reaction to competitive incentive schemes, may have only limited applicability to farmers in the United States or even the general population in Austria. It may not even help assess the importance of competitiveness for observed wage differences or work choices of Austrian farmers, if the experimenter was not able to manipulate those choices. Second, field evidence, while often compelling, may be hard to come by when considering existing data. There are, of course, always exceptions, such as the work by Ors, Palomino, and Peyrache (2013) mentioned earlier. To assess the external relevance of gender differences in competitiveness, it will be useful to find, or create, databases that combine a good measure of competitiveness with field outcomes. This is exactly the aim of Buser, Niederle, and Oosterbeek (BNO; 2014). They investigate gender differences in education choices of ninth graders in the Netherlands. Specifically, children who go to the preuniversity school in the Netherlands share the education experience in the first 3 years, grades 6–9, and are somewhat randomly assigned to classes. At the end of ninth grade, children select 1 of 4 possible academic tracks, best described as mathematics, biology, economics or literature, for their last three years of high school. This is the ordering of how math and science intensive the education in each track is. It is also the ordering of how prestigious the tracks are, where the best students go, and how likely they are to actually go to university later. BNO conduct experiments with every ninth grader from 4 schools in and around Amsterdam. The in-class experiment consists of a slight variation of NV: children add up sets of 4 two-digit numbers for 3 minutes, first under a piece-rate scheme and then a tournament scheme, where they compete against 3 classmates who were randomly selected by computer after the end of the experiment. Round 3 implements the NV choice of compensation scheme, tournament or piece rate. A participant who selected the tournament would win if her or his new round 3 performance exceeded the round 2 performance of her or his 3 competitors. BNO assess the students’ beliefs about their relative round 2 tournament performance and their risk attitudes. BNO also measure each student’s beliefs about their subjective mathematical ability, as well as how they rank the four study tracks in terms of the question, Which track do the best students pick?

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The roughly 400 children in BNO exhibit behavior that mirrors that of all children of the Netherlands concerning their education choices. Children to a large extent agree that the order of prestige of academic tracks corresponds to their math and science intensity, and children who chose more prestigious tracks have a higher GPA. To assess academic track choices of students, BNO control not only for objective academic ability as measured by grades, but also subjective academic ability as measured by the students’ beliefs about how easy mathematics is for them, as well as how good they are in math compared to their peers. Ordered probit regressions show that being female accounts for 15% of the distance between choosing the most and the least prestigious tracks controlling for grades. To provide a measure of the importance of the female dummy, note that a one standard deviation in GPA accounts for only 11% of the gap between choosing the most and least prestigious tracks. The children also exhibit tournament-entry decisions that mirror the results in NV: Controlling for performance, girls are about 23 percentage points less likely to enter the tournament. Slightly over 30% of this gender gap can be explained by gender differences in confidence. Risk attitudes, whether measured by a lottery choice or a simple questionnaire item significantly predict tournament entry, but reduce the gender gap in competitiveness only by a small amount once confidence is controlled for. To assess the importance of competitiveness on academic track choice, note that the binary variable of tournament entry (controlling for performance in the experimental task, as well as grades and the subjects’ beliefs about their academic ability) accounts for 18% of the gap between choosing the least and most prestigious track (compared to 15% for being female). That is, a student’s competitiveness is a slightly better predictor of academic track choice than gender. When controlling for both gender and competitiveness, the gender difference drops from 15.4 to 12.3 percent, a statistically significant change. BNO therefore find that 20% of the gender gap in choices can be accounted for by gender differences in competitiveness. Since tournament entry is partially explained by confidence (the belief about the guessed tournament rank) and risk aversion, BNO assess the extent to which they drive the importance of tournament entry on study track choices. Let net competitiveness be the residual of a regression of tournament entry on the measures of performance in the experiment, the guessed rank and the risk measures. Figure 8.4 shows for each track the average net competitiveness of boys and girls that chose that track. For each gender, more competitive students select more prestigious tracks. This provides a first indication that the effect of competitiveness on study track choices is not due to the impact of risk attitudes and beliefs about relative performance (or confidence) alone. BNO provide ordered probit regressions that control for the students’ risk attitudes as well as their confidence. Tournament entry in the experiment reduces the gender gap in track choices by 16% (compared to 20% without confidence and risk controls). Together, competitiveness and risk measures reduce the gender gap in track choices by 33%. The effect of risk only is 16%, and that of competitiveness only is 20%; hence, the combined effect (33%) is 92% of the sum of the separate competitiveness and risk effects. This suggests that competitiveness and risk attitudes have almost orthogonal effects on the gender gap in track choices. Controlling for beliefs via the guessed tournament rank actually increases the gender gap in choices. Controlling for competitiveness, risk, and confidence reduces the gender gap in choices by only 26%. BNO then argue that tournament entry is indeed a measure of the students’ competitiveness rather than an (additional) measure of the students’ perceived math ability, their actual math ability, or their preference for math.

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Two other papers address the external relevance of competitiveness on education choices. Zhang (2012a) conducts NV-style experiments with middle school children from Ninlang County in China. Zhang also observes the students’ decision to take a very competitive high school entry exam. Controlling for test scores on a previous exam, students who are more competitive are more likely to take this entry exam. However, Zhang finds no gender gap in tournament entry or in entry rates of taking the exams. Note that Zhang (2012 b) does find a gender gap in tournament entry for ethnic minorities among high school children from the same area. The second paper, Reuben, Wiswall, and Zafar (2013), finds that among NYU students, competitiveness (as well as overconfidence, though not risk aversion) is positively correlated with earnings expectations. Furthermore, about 18% of the gender gap in earnings expectations can be accounted for by gender differences in competitiveness and overconfidence. As in BNO, this paper finds that the experimental variables are important, even when including various control variables such as test scores and family background. However, while expected earnings are related to major choices, Reuben and others do not find that the experimental variables are related to choice of major. Note, however, that there is no obvious ranking of majors, while obvious rankings were available for BNO and Zhang. More recently, Reuben, Sapienza, and Zingales (2015) show a correlation between competitiveness and earnings of MBA graduates. Overall, there is clearly more work to be done to confirm the external relevance of competitiveness as an independent trait, a trait that can account for education choices and also other labor market choices. To conclude, gender differences in competitiveness provide a model for how new laboratory findings found their way into more mainstream economics. This has been achieved first by an important phase of experimentation with lots of replications and

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checks for the robustness of results, as well as trying to understand how competitiveness differs from other traits such as confidence and risk aversion. The most important step has been not only to conduct field experiments, but to create data sets that include both laboratory and field measures. While this last step is somewhat new, it is helpful to show that gender differences in competitiveness can help account for gender differences in education and labor market outcomes.

III GENDER DIFFERENCES IN SELECTING CHALLENGING TASKS AND SPEAKING UP Gender differences in competitiveness and preferences over incentive schemes have received a lot of attention. This literature has also been successful in showing that competitive attitudes predict, for example, education choices of students. Specifically, Buser, Niederle, and Oosterbeek (2014) showed that students who are more competitive select more math intensive and more prestigious study profiles. However, there has been little work in assessing directly to what extent women and men differ in selecting challenging or difficult tasks and how those differences could be mitigated. For example, male and female undergraduates differ significantly in the rate with which they select to be STEM and economics majors. Therefore, it may be important to understand whether women, in general, shy away from challenging tasks and whether (or what) institutional changes can affect these choices. In this section I first review papers that tackle gender differences in task choices where tasks can be ordered in how challenging they are. I then discuss which, if any, institutional changes may affect those choices. I then present papers that address whether women may be more reluctant to speak up and put themselves forward. III.A Gender Differences in Task Choice A first indication that women shy away from challenging tasks compared to men can be seen from a final treatment in Gneezy, Niederle, and Rustichini (2003). Women and men could decide upon the task difficulty (mazes from level 1 to 5), where level x would be remunerated at x shekels for each completed maze (with 4 shekels equal about $1). All participants only saw one level 2 maze before making the decision. Men chose significantly more difficult levels than women. The average choice was 3.4 for males and 2.6 for females, a significant difference. There are, however, two limitations in interpreting this experiment. First, neither the authors nor the participants knew what the optimal choice would be for someone who has a high ability in solving mazes compared to someone of low ability. It could be that for everyone, earnings are highest at task difficulty 3. Second, even if it were true that higher-performing participants have on average higher earnings from choosing harder mazes, participants did not know it. Another early work showing gender differences in task choice is by Huberman and Rubinstein (2001, 6). Their abstract describes the setting of their experiment very well: “We asked subjects to self-select into one of two contests, ‘coin’ or ‘die.’ The winner in each of the contests is the person with the most correct guesses of 20 coin flips or 20 rolls of a die, respectively. The majority of subjects reported that they believed that most people would go to the ‘coin’ group. They were correct. Although the right action under this belief is to choose ‘die,’ most people chose to be with the majority. Both men and women tended to make this mistake, but women’s propensity to err in this particular experiment was stronger. This is puzzling as our overall impression (based

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on preliminary experiments which were not documented scientifically) does not support the existence of gender differences in other strategic situations.” The attraction of a pure “guessing” task is that neither one’s own ability nor the ability of others matters for the performance in the task. The main result of their experiment is that “Women behave less ‘rationally’: Only 15% of the women vs. 35% of the men act optimally on their beliefs (including wrong beliefs)!” Bracha and Fershtman (2014) have participants allocate time within 10 minutes between a mindless filing task—deciding whether a number is odd or even—and a more challenging sequence task, where subjects are given 3 numbers and have to fill in the missing fourth number. They find that under a piece-rate scheme, women spend less overall time on the challenging task, more time per question, though with an overall similar success rate per question. Under a tournament incentive, both women and men reduce the time spent on the challenging task, though their overall performance is the same as under the piece rate. Interestingly, the success rate of women declines significantly, and significantly more so than that of men, when performing in the tournament compared to the piece rate. This effect is mostly present in the last 3 minutes of the 10-minute performance. Finally, Niederle and Yestrumskas (2008), combines two of the previous approaches. First, one task is “objectively” harder than another (as in Gneezy, Niederle, and Rustichini, 2003). Second, as in Huberman and Rubinstein (2001), the environment is one where both the experimenter and the subjects know what task is payoff maximizing for whom. Niederle and Yestrumskas (2008) study whether women shy away from difficult and challenging tasks more than men and what institutional changes can alleviate these gender differences in choices. The objective is to assess whether a woman and a man of the same performance level make different choices. To that aim, Niederle and Yestrumskas (2008) create an environment such that participants can be divided into two groups, one of which, given their ability, has higher earnings from the challenging task, while the other has higher earnings from the easier, nonchallenging task. Specifically, the task is solving mazes on paper for 10 minutes. They have an easy task (easy mazes at $0.50 per maze) and a hard task (hard mazes, with a kinked incentive scheme: $0.25 for each of the first 4 mazes and then $3.50 for each additional one). This creates two tasks in which it is the case that participants can be divided into two performance levels, high and low. The paper shows that high-performancelevel participants have higher earnings from the hard task, while low-performancelevel participants do so from the easy task. The reason is that low- performance-level participants simply do not solve sufficiently many hard mazes to reach the steep part of the piece-rate incentives. Furthermore, each participant’s performance level can be identified by their first performance in the easy task where approximately the top 40% performers in this first easy task are of high performance level, specifically all participants who solved 11 easy mazes or more. In each treatment, participants first perform the easy task. This allows the experimenter to determine the performance level of each subject. Participants then choose the task difficulty for the next 2 tasks. When deciding about the task difficulty for the last 2 rounds, participants always know that a high performance participant, one who was among the top 40% of all participants in the initial easy task, has an expectation of higher earnings from a subsequent hard task, while others have higher expected earnings from a subsequent easy task. That is, participants, while not knowing their own performance

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level, know that the labels hard and easy task were meaningful. Participants were paid for their first performance and 1 of the 2 subsequent performances. A first group of subjects, who determine the validity of the high- and lowperformance classification, were asked about their relative performance and show no gender differences in beliefs about their relative performance. The first main treatment, Choice, has participants choose the performance level for the next 2 tasks after their initial task 1 performance. While every single highperforming man chose at least one hard task, only 65% of women did. On average, 86% of high-performing men chose the hard task compared to only 57% of women. On the other hand, 88% of low-performing men chose 1 hard task, compared to only 58% of low performing women. Low-performing men chose the hard task with 70% chance, compared to 42% for low-performing women. Conditional on the performance level, women choose the hard task significantly less often than men, results that mimic those of gender differences in choices of competitive incentive schemes. One (boring) explanation for this gender difference could be pure task preference: men more than women prefer the hard task. In the feedback treatment, participants receive information about whether they are of high- or low-performance level. If pure task preference were the major driving factor, choices of women and men should not change much. However, once subjects learn their performance level, every single high-performing subject, male or female, chose at least one hard task. Furthermore, high-performing men chose the hard task with certainty, that is, every single highperforming man chose the hard task twice, while women chose it with 86% chance. Low-performing men chose the hard task with 25% chance, compared to 28% for lowperforming women. That is, when subjects learn their performance level with certainty, men and women do not differ much in their choices anymore. High-performance-level participants choose the hard task, and others choose the easy task. However, as an institutional design, it may be quite unrealistic to have a perfect diagnostic exam of the performance level of a subject. The paper then describes another institutional change that could be implemented in situations where people have to choose between an easier and a more challenging option: allowing participants to make gradual choices as opposed to choosing the difficulty for the next 2 tasks immediately, as in the Choice treatment. In the reduced commitment treatment, after the first easy task and after learning of the calibration, participants make a choice of difficulty level for their second task and perform. Only afterward do participants decide on the difficulty level for their third and final performance. This treatment results in high-performing participants mostly to choose the hard task: 88% of high-performing men and 89% of high-performing women choose at least one hard task, and both high-performing men and high-performing women have an 81% chance of choosing a hard task. That is, high-performance-level participants mostly choose the hard task, and there are no gender differences in choices among those subjects. The situation is different for low-performing participants. While low-performing women mostly choose the easy task (which is payoff maximizing for them), this is not the case for low-performing men. Low-performing men have a 72% chance of selecting the hard task, compared to 28% for low-performing women. Overall, gradual choices help high-performing women to choose the hard and challenging task. Note that gradual choices do not help low-performing men to avoid the hard task. One possible explanation could be that the information received from performing in the hard task is less precise, that is, it is harder to learn that the hard task choice was not the money-maximizing one. The reason is that participants improve

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their performance in the easy task as well. Comparing earnings from the hard task in round 2 to those made when performing the easy task in round 1 biases results toward higher earnings for the hard task. This final treatment also shows that the reason for gender differences in task difficulty in the initial Choice treatment was not due to an aversion to learning one’s type. It could be that the results were driven by the fact that women may be more risk averse (and hence, for given beliefs, do not choose to enter the hard task that has higher variance in pay) or less certain in their beliefs of being a high performer or that an initial performance is indeed indicative of a high-performance level. Overall, there seem to be gender differences in task choices when one task is clearly easier than the other, with women being more likely to choose the easier task. Note that in the case of Huberman and Rubinstein (2001), the easy task would have to be the one in which a “better” performance is easier, though in this seemingly easier task the expected earnings are lower. In that sense, the task in which it is easier to win is the task in which it is harder to guess the exact right answer. In the earlier psychology literature, there is an example, Dweck (2000), that proposes a mechanism of who may be more reluctant to engage in challenging tasks and why females may be overrepresented in this group. Specifically, the hypothesis is that there are two extreme views of intelligence, or talent for a specific subject area. One is that intelligence is a fixed trait and tests, and the like, can basically uncover how talented someone is. Another view is that intelligence is like a muscle, something that increases as it is exercised. The more someone believes that intelligence is fixed and the person has already been reinforced that she or he is intelligent, the more the person may shy away from challenges. After all, there is a chance to learn that perhaps the challenge leads to failure. On the other hand, if intelligence is like a muscle, initial failure from challenges may not be a problem, since it is understood that only by keeping at it can we improve. The gender component is that females are more likely to hear that they are smart early in their education, so females may shy away more from challenges than males. An interesting avenue for future research could be to better understand the interplay between gender differences in choices and different institutional designs that either exacerbate or reduce these choices. This question came up in the last section on gender differences in competition, when I discussed the external relevance of competitiveness. Buser, Niederle, and Oosterbeek (2014) showed that competitiveness predicts educational choices in the Netherlands. The Netherlands, like many continental European countries, has children make educational choices in a “once-and-for-all” choice setting: children make one choice that determines their education for several years. These choices are not flexible like in the US school system, in which students are much more likely to make gradual choices. A choice of one hard mathematics class does not preclude not choosing it in the next semester. While research mentioned before hints to the fact that gradual choices may increase the chances of women selecting challenging tasks, it clearly remains a very open question as to what extent different choice architectures affect choices of women and men. III.B Gender Differences in Speaking up The final set of papers I present in this section considers whether women are as willing to speak up as men are. While there is a psychology literature on behavior in teams and whether women have less influence than men, the problem with that literature is that there are many biases that can account for potential gender differences in

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influence: women may not only behave differently, but also may be treated differently (see Thomas-Hunt and Phillips (2004) and references therein). The papers I discuss share the feature that participants retain some anonymity and don’t have to worry about immediate dismissal. The focus is, rather, on the decision to give advice or contribute an idea. Cooper and Kagel (2013) consider whether there are gender differences in the propensity to give advice, and Coffman (2014) considers whether there are differences in the propensity to speak up when deciding which team member should answer a question. Cooper and Kagel (2013) study advice giving in the context of a signaling game that is based on the Milgrom and Roberts (1982) entry limit pricing game. The crux of the game is that the high-quality sender has to recognize that they can signal their type via a separating equilibrium. Cooper and Kagel characterize this as a “eureka”-type problem, in which there is a clear insight that is easily explained to others. In the first of their three main treatments, the 1 × 1 treatment, one player plays against another. In the 2 ×2 treatment, subjects are paired with one another and interact in two-person teams.23 In the advice treatment, subjects play in 2-person teams, with one subject receiving the role as advisor and the other as advisee. “Advisors and advisees played the limit pricing game separately, with no need to agree on a common action (and no mechanism for doing so). Advisors had (almost) continuous access to a messaging program which they could use to send advice to their advisee” (Cooper and Kagel 2013, 9). Advisees could not communicate with advisors and could not observe the play of advisors. Advisors “received a bonus equal to 30% of their advisee’s total payoff (along with their own payoff). These bonus payments were only reported at the end of an experimental session so that advisors could not tell what choices their advisees had made.” The main question is whether there is a gender difference in both giving and taking advice. Earlier work (Cooper and Kagel, 2007) showed that teams play better than individuals, even when considering the truth-wins norm. Specifically, forming artificial teams out of individual players and having them play strategically if one of the individuals plays strategically still leads to less strategic play than is observed in actual teams that are allowed to communicate with one another. The reason is that teams have an easier time “putting themselves in the shoes of the other” and hence understanding that the other player may make inferences from and react to one’s own choices. The present paper shows that “having an advisor significantly increases the frequency of strategic play, especially when the advisor plays strategically. But the effect is weaker than would be predicted by a truth wins model where advisees play strategically if either they or their advisor figure out strategic play.” This is due partly to the behavior of advisors, where they find large gender differences, and partly due to the behavior of advisees, where there are essentially no gender differences. First, females are less likely to play strategically than males. Therefore, to compare the behavior of advisors, the paper focuses on advisors who have played strategically. “[A]lmost half (43%) of advisors who have a history of playing strategically fail to advise their partners to play strategically. This cannot be attributed to a general unwillingness to send messages or give advice, as 93% of . . . advisors send at least some message and 85% send messages that include advice how to play . . . [a total of] 41% of . . . advisors who play strategically during the first half of their session never advise their partner to play strategically” (Cooper and Kagel 2013, 4). This effect is to a large extent driven by female advisors. “Seventy three percent . . . of . . . male advisors who have played strategically also give advice to play strategically, compared to only 31% of female advisors.” To account for the aforementioned gender differences, Cooper and Kagel note that “Given that cognitive ability is basically identical for men and women in our sample,

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we conjecture that relatively low adoption of strategic play by women reflects lower confidence in their insights.”24 In terms of behavior of advisees, a third (34%) of those who have received advice to play strategically fail to follow that advice. Furthermore, “[s]ubject to being advised to play strategically, the marginal effect of a sound explanation as to why this advice should be followed is essentially zero” (Cooper and Kagel 2013, 2). There are, however, basically no gender differences in advisees; while women are somewhat more receptive to advice than men are, this difference is not significant. This reluctance of women to “trust” in one’s answer and put oneself forward is also found by Coffman (2014). Her paper considers whether women and men differ in their propensity to be present or speak up and have their opinion or answer determine the answer for the whole group. She studies how this varies depending on whether the task is a task where participants expect males to be better than females, or vice versa. Specifically, participants first answer a set of multiple-choice questions in 6 categories that vary in how male- or female-typed they are, as declared by the beliefs of participants whether in general, in this category, “women know more” or there are “no gender differences” or “men know more.” Participants are then put in groups of 2 and decide how willing they are to contribute their answers to new questions in these categories to their group. Specifically, participants chose a position in line, from 1 to 4, where the participant with the lower position is the one providing the answer for the group. In case of ties the answer of one group member is chosen randomly. For female categories, women are more likely to contribute their answers than men are, and for male categories, the opposite is true. Controlling for ability, women become less likely and men become more likely to contribute answers to the group as the maleness of the category increases. A big part of this effect is driven by gender differences in beliefs: compared to men, women believe they have a higher chance to answer a question correctly in female categories, while the opposite is true in male categories. Controlling for beliefs and ability, there are no gender differences in contributing answers in the female categories. However, in the male categories, even after controlling for beliefs and ability, women are less likely to contribute their ideas than men are (i.e., choose a higher position in line). Coffman (2014) then addresses whether providing participants with feedback (i.e., whether or not they were the person in the group who had the highest score in a given category) can encourage high-ability members to contribute. However, “we find only weak evidence that feedback increases willingness to contribute among knowledgeable group members.” Overall, there seems to be a gender difference, with women being somewhat reluctant, compared to men, to speak up, especially in tasks where stereotypes are that men are better. In both papers I presented, this results in considerable inefficiencies. Overall, this section is relatively short but is one I think that should be much longer. Understanding what drives women and men to “be present and show up” for challenging and perhaps stereotypical male tasks, to speak up and have their opinion count, needs to be better understood. It will also be important to understand what institutional changes can level the playing field.

IV ALTRUISM AND COOPERATION One of the traits for which gender differences are generally assumed is altruism and cooperation—with women supposedly being more altruistic and cooperative.

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The corresponding view is that women are more caring and nurturing and more likely to help. For example, Eagly and Crowley (1986) write that, “The female gender role includes norms encouraging certain forms of helping. Many . . . have argued that women are expected to place the needs of others, especially those of family members, before their own. Gilligan (1982) has identified this theme as women’s orientation toward caring and responsibility.” Interestingly, an early meta-analysis in psychology on gender and helping behavior (Eagly and Crowley 1986) found that in about 100 studies, men helped on average more (Cohen’s d = 0.34).25 In this section I focus on two prominent ways economists have assessed gender differences in altruism and cooperation. The first concerns distributional preferences, over income, of women and men. These are often studied using versions of dictator games, where one person, the dictator, decides how to distribute money among a set of participants, in general the dictator and one other person (Forsythe et al. 1994). A second way in which altruism has often been looked at is by studying cooperation in prisoner’s dilemma, public good, or social dilemma games. In principle, when considering behavior in games, motives besides altruism or cooperativeness may also play a role. However, these games share the feature that in the one-period version, they have a dominant strategy (to defect in a prisoner’s dilemma, not contribute to the public good, or consume massively, respectively). So, at least in theory, strategic motives play no role. Of course, in practice, there are many reasons, besides altruistic or cooperative motives, why behavior does not correspond to the dominant strategy. For example, the one-shot public good and dictator games share the feature that the dominant strategy is at the corner of the action set (contributing nothing). Giving positive amounts may therefore reflect confusion rather than deliberate altruistic choices. There has been some evidence that changes in the action set changes giving in the dictator game; see, for example, Bardsley (2008) and, in a very close design, List (2007).26 Likewise, Recalde, Riedl, and Vesterlund (2014,) using public good games where both the dominant strategy equilibrium and the efficient outcome are in the interior, show that a considerable amount of behavior is due to confusion.27 There is, however, no evidence that women are more confused than men in such simple decisions, so we will ignore the possibility that gender differences in altruism or cooperation in these games are due to gender differences in confusion.28 Another reason for giving in those simple games could be image concerns. Andreoni and Bernheim (2009) provide evidence that participants give in a dictator game not only because participants are altruistic or fair, but also because they like to be perceived as fair. Assessing the impact of image concerns in these games remains a lively and, as of now, still unresolved debate. Most recently, Exley (2014) finds that women are more image conscious than men (see also Jones and Lenardi 2014). We will, however, ignore this issue as well. Other games used to assess gender differences in social preferences are the ultimatum game (Güth, Schmittberger, and Schwarze 1982) and the trust game (Berg, Dickhaut, and McCabe 1995).29 Croson and Gneezy’s (2009) survey on gender differences review these games in the section on differences in social preferences. Ultimatum and trust games do not have a dominant strategy, though in both, the unique subgame perfect equilibrium is for the first mover to not pass any money (or, for the discrete ultimatum game, at most the smallest unit) to the second mover. However, especially for the ultimatum game, the subgame-perfect equilibrium strategies of the first mover result in rather low payoffs (empirically) compared to the payoff-maximizing strategy. Therefore, gender differences in these games may to a much larger extent reflect gender differences

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in beliefs about the behavior of other player(s) or in how strategically sophisticated players are rather than gender differences in altruism and cooperation. As a consequence I will not review these games.30 A METHODOLOGICAL ASIDE: COHEN’S d Much of the material in this section and in the next section on risk preferences involves work published in both the economics and psychology literature. In the latter there is frequent reference to Cohen’s d,which is used to evaluate the importance of differences between means (as opposed to just their statistical significance). It is probably the formal equivalent in psychology to the common notion in economics of whether a difference in means is “economically meaningful.” It is used as a measure of effect size when comparing the mean of one sample to another and is defined as the difference in population means (μ1 – μ2 ) divided by the population standard deviation σ , which is supposed to be common among the two populations; that is, d=

μ1 − μ2 σ

In practice, Cohen’s d is computed as the difference in sample means X¯ 1 − X¯ 2 divided by the pooled standard deviation, s , where s is computed as  s=

(n1 − 1)s 12 + (n2 − 1)s 22 n1 + n2 − 2

where s i2 is the variance of the sample i = 1, 2, each with sample size ni for i = 1, 2, that is, i 1  (xi,k − x¯ i )2 ni − 1 k=1

n

s i2 =

Cohen’s d is the standardized difference between two population means, here mostly male versus female population means. Cohen (1988) provides a guideline for how to think of effect sizes that is used to describe many psychological effects: An effect size of 0.2 is considered small, of 0.5 is medium, and anything of 0.8 or larger is considered a large effect. There are several ways in which to interpret Cohen’s d. First, assuming normal distributions, a specific effect size helps determine the minimum sample size required to get a significant result (say, 10% in a 2-sided test) with certain power (say, 0.8—that is, there is an 80% chance that we correctly reject the null when it is false). Second, Cohen’s d can give an indication of how likely it is that a person from sample 1 (male) has a higher “outcome” than a person from sample 2 (female). Third, Cohen’s d can give an indication of how much of the variation in the outcome can be accounted for by gender. With a Cohen’s d of 0.2, there is a 56% chance that a randomly chosen man has a higher outcome than a randomly chosen woman, with 1% of the variation in outcomes accounted for by gender. With a Cohen’s d of 0.5, there is a 64% chance that a randomly chosen man has a higher value than a randomly chosen woman, with 6% of the variation in outcomes accounted for by gender.

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0.5 Men (46 observations) Women (31 observations)

Frequency

0.4 0.3 0.2 0.1 0

0

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3 Gift ($)

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Figure 8.5: Dictator giving by gender: amount left for recipients (pooled data). Source: Bolton and Katok (1995).

With a Cohen’s d of 0.8, there is a 71% chance that a randomly chosen man has a higher value than a randomly chosen woman, with 14% of the variation in outcomes accounted for by gender. To give some examples of gender differences and their effect sizes, Hyde (2005) presents a survey over major meta-analyses of research on gender differences. She covers 44 papers, with a total of 124 effect sizes analyzing cognitive variables, communication, social, and personality variables, psychological well-beings, motor behavior, and some other traits. Only a particular motor skill—throw velocity as well as distance—has a Cohen’s d of about 2 (Hyde 2005). Seven more variables have a Cohen’s d of 0.66 or higher, namely, grip strength, attitudes about casual sex, masturbation, mental rotation, mechanical reasoning, agreeableness, and tender-mindedness (the only one where women score higher). Almost 80% of effect sizes are less than 0.35. IV.A Dictator-Style Games An early dictator game paper that examines gender differences in social preferences is Bolton and Katok (1995). They consider various dictator games over $10, pooling data from different treatments, with a total of 46 male and 31 female participants.31 Subjects were not aware of the gender of their partners. Probably the best summary of their data is Figure 8.5, which shows, for each amount passed to the other player (from 0 to 5), the fraction of women and men, separately, who passed that amount. They conclude that, “We find no evidence for gender differences in generosity.” The next paper in this literature, Eckel and Grossman (1998), finds a very different result. They have students divide $10 in a double blind way, in an effort to avoid potential experimenter-demand effects. One drawback to this procedure is that it requires single-sex groups, since they can’t attribute any choice to a specific person. Table 8.1 shows the distribution of outcomes. There are significant gender differences, with women giving more: $1.60 versus $0.82 ( p < 0.01) for men. They conclude that, “The double-anonymous dictator setting removes risk, the possibility of gender-related subject interactions, and the experimenter effect, leaving

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Women

Men

$0 $1 $2 $3 $4 $5 $6 $7 $8 $9 $10

46.67 10.00 13.33 11.67 3.33 15.00 0 0 0 0 0

60.00 26.67 3.33 5.00 0 3.33 0 0 0 0 1.67

Average donation Observations

$ 1.60 60

$ 0.82 60

only underlying selflessness as an explanation for donating money. Our results indicate that women are less selfish than men when confounding factors are eliminated” (pp. 732–33). Given that there are many differences between these two studies, it would be too hasty to conclude one way or the other whether gender differences in altruism exist and whether they are altered when participants interact in single-sex compared to mixedsex groups. This early work perhaps also drives home the point that replications, as well of investigations of robustness, are extremely important (Coffman and Niederle 2015, 2016). The first paper to offer a more comprehensive study on gender differences in dictator games is Andreoni and Vesterlund (2001). They ask a total of 142 subjects (95 men, 47 women) to decide how to allocate a fixed amount between themselves and another person, where they vary the budget to be allocated as well as prices between own and others’ payoffs. Subjects make 8 different choices, where the budgets in tokens are 40, 60, 75 and 100, and the value of tokens for the two players range from 3:1 to 1:3. For a 3:1 value, each token is worth 3 points for the dictator but only 1 point for the recipient, meaning that giving is expensive. For each subject, 1 of the 8 allocations was chosen for payment, where each point was redeemed at $0.10. In three decisions tokens were worth more to the dictator, but in three the exchange rate was reversed so they were worth more to the recipient; in 2 decisions the exchange rate was 1:1. Across the 8 decisions, men on average passed $2.56 to the other player compared to $2.60 for the women, with the difference not significant. However, these similar averages mask important heterogeneity. Figure 8.6 shows, for each price of giving in { 13 , 12 , 1, 2, 3}, the payoff passed to the other player as a fraction of income the dictators would have received had they kept all the tokens. For prices of giving below 1, the payoff men pass to the other player is a higher fraction of their income than it is for females. In fact, for a price of 13 , men pass more to the other player than they could have secured for themselves if they had kept everything; that is, men are more generous than women when giving is cheap. However, when giving is expensive (for prices of 1 or more), women are more generous than men. Figure 8.6a nicely illustrates that the curve for

Gender

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Male Female

0.5

2

Females

Frequency

Price

517

0.6

3

1.5 1

0.4 0.3 0.2

Males

0.1

0.5 0

•

0

0 25 05 0.75 Fraction of income

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0

Selfish

Leontief

Perfect substitutes

Figure 8.6: (a) Payoff passed as a fraction of income. (b) Preference distribution (strong and weak). Source: Andreoni and Vesterlund (2001).

men is flatter than for women, meaning that the amount of money passed as a fraction of income is more sensitive to price for men than it is for women. Andreoni and Vesterlund (2001) then classify individual subjects as either totally Selfish, Leontief—utility is the minimum of the subjects’ own payoff and the others’ payoff—and Perfect Substitutes—where subjects treat own and other payoff as perfect substitutes, that is, allocate all tokens to the person with the highest redemption value. Roughly 44% of subjects exactly fit one of these categories, with the remainder allocated to these categories using the Euclidian distance between actual behavior and the behavior predicted by one of those utility functions. Figure 8.6b shows the fraction of women and men for each type, where the two distributions are significantly different. Compared to women, men are more likely to be selfish or to have a utility function that views payoffs as perfect substitutes, consistent with maximizing total payoffs regardless of who receives the money. Women, on the other hand, are more likely to aim for payoff equality. One early summary of gender differences in altruism and cooperation is Eckel and Grossman (2008). In addition to summarizing the results of the three dictator game experiments just discussed, they look at responder behavior in ultimatum games. Eckel and Grossman (2001) find that women are less likely to reject offers, especially those made by other women. In contrast, Solnick (2001) did not find this result using the strategy-method version of the ultimatum game and the behavior of one “punishment game.” Given these results, Eckel and Grossman (2008, section 4 conclusions) conclude, “In those settings where subjects are not exposed to risk—i.e., as respondent in ultimatum experiments employing the ‘game method’ design and dictator games— systematic differences are revealed. The choices women make are less individuallyoriented and more socially-oriented.” Several other early papers explicitly study the interaction of the gender of the dictator and recipient. In Dufwenberg and Muren (2006), 352 dictators divide income between themselves and another student described as a randomly selected female (or male)

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student. While they find that women receive significantly more than men, donations do not differ between men and women. Ben-Ner, Kong, and Putterman (2004) find quite different results: They have 154 dictators and find that information on the recipients’ gender does not affect giving for men, but it does for women (who give less to women). Largely as a result of this, they find that overall, women give less than men, though the difference fails to be statistically significant. Houser and Schunk (2009) have German children between 8 and 10 divide M&Ms between themselves and a child at another school. In all the 3 treatments, the name of the child who ends up with the most M&Ms is announced to the whole class by writing it on the blackboard. In addition in treatments 2 and 3, this child also receives her or his favorite hand stamp. In treatment 3 (but not in treatments 1 and 2), dictators are told the gender of the child with whom they are paired. While in treatment 1, boys and girls send the same amount, around 8.5 (out of 20), the amount of M&Ms given is reduced in treatment 2 for boys, who now give only 5.2 M&Ms, which is significantly less than before and significantly less than girls give (around 9 M&Ms). In treatment 3, boys give around 5.6 M&Ms, while girls give 8.9, replicating the effect of treatment 2. Furthermore, boys send on average 2.1 fewer M&Ms to girls than to boys (though the difference is not significant, p > 0.10), with girls also sending fewer M&Ms to girls, a smaller average effect (1.9 fewer M&Ms) but one that is significant ( p < 0.05). Although this difference in giving between boys and girls to girls is very unlikely to be statistically significant, Houser and Schunk (2009, 638) write, “While not comparable due to the influence of competitive pressure in our third treatment, this latter finding seems to contrast with findings from adult samples. In particular, both Holm and Engseld (2005) and Dufwenberg and Muren (2006) report men generally receive less than women when information regarding one’s receiver’s gender is available. The main finding from the three treatments is that competition decreases fairness for boys but not for girls.” Croson and Gneezy (2009), in their section on dictator games, summarize nine studies. These include the three dictator games summarized by Eckel and Grossman (2008b) just described, three games that are somewhat different from dictator games (e.g., one has a disinterested third party make allocations), and the three dictator games just described that explicitly study the interaction of the gender of the dictator and recipient. They summarize this literature as “men choose efficient allocations while women are more inequality averse.” Their paper then addresses whether donations by women are more dependent on the sex of the recipient than donations by men. “However, comparisons between the first two studies (Eckel and Grossman 1998; Bolton and Katok 1995), and within the final two studies (Ben-Ner, Kong, and Putterman 2004; Houser and Schunk 2009), suggests that women’s decisions are more context specific than men’s.” General conclusions of this sort would appear to be premature. Recall that Dufwenberg and Muren (2006) do not find gender differences in giving. Furthermore, while Ben-Ner, Kong, and Putterman (2004) and Houser and Schunk (2009) find that women react to the recipients’ gender and men do not, neither paper finds that women react to the recipients gender significantly more than men do. In fact, one could argue the opposite, namely, that the behavior of men is more context dependent than women, since (1) giving for men depends more on the price than for women (Andreoni and Vesterlund 2001), and (2) Houser and Schunk (2009) found that boys are much more inclined to become less prosocial than girls when competitive pressure is induced. Of course, arguing that the behavior of men is more context dependent than that of women would be equally premature, given the small number of papers surveyed up to this point.

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A more recent summary of the dictator game literature is provided by Engel (2011), a meta-analysis covering 129 dictator papers published between 1992 and the end of 2009.32 Summarizing demographic variables, he writes that (p. 597), “Since in ordinary papers on dictator games gender is not reported, meta-regression with all data would not be meaningful. If one confines the sample to those papers that have explicitly tested gender, it turns out that women give significantly more . . . ” since men give on average 21% of the pie to the other participant, while women give on average 27% (difference that is significant at the 10% level). Note, however, that only 12 papers, 10% of the surveyed dictator games, explicitly test for gender effects of the dictator. Unfortunately, Engel makes no attempt to assess whether there is any reporting bias, that is, whether papers selectively decide whether to report results on gender. Clearly, if gender results are reported more often when they conform to the view of existing summaries of the literature, the result that women are more generous may be derived from a biased sample. While Engel includes Andreoni and Vesterlund (2001), it is not clear how that paper is coded in this meta-analysis. Engel (2011) also discusses whether women receive more than men do: “Women do not only give more in dictator games, they also get more as recipients. In a metaregression confined to those experiments that have explicitly tested recipient gender, this factor alone explains 73.2% of the observed variance, . . . ” with male recipients receiving on average only 5% of the total pie compared to women, who receive about 20% of the total pie, a difference that is significant at the 1% level. He goes on to note that “If one controls for recipient gender, dictator gender is insignificant . . . .” Given that the number of papers covered in this subsection (over 30) is larger than in the previous subsection (12) and Engel does not provide a table on how each paper is coded, it seems that in the present regressions, all papers are included that have a gender variable, even if they have single-sex groups. One summary of Engel (2011) may be that women are more generous than men are. However, a more careful analysis reveals that, conditional on the recipient of the gender, there is no significant difference in giving between women and men. While an overall statement of whether males or females are more generous seems not to be clearly supported by the data on dictator games, the result that giving by men depends more on price than that by women might be. Papers that replicate the Andreoni and Vesterlund (2001) result that males are more efficiency oriented while females are more focused on equity—that is, giving by men is more price elastic—include Visser and Roelofs (2011), Boschini, Muren, and Persson (2012), and Fisman, Jakiela, and Kariv (2014). Papers that find directional, but nonsignificant, results include Leider et al. (2009) and Balafoutas, Kerschbamer, and Sutter (2012). Cox and Deck (2006), often cited as refuting the Andreoni and Vesterlund result, do not, in fact, vary the price of giving in their experiments.33 IV.B Field Evidence and External Relevance of Gender Differences in Giving I confine myself to discussing the field evidence with respect to the gender gap in the elasticity of giving. Andreoni and Vesterlund (2001) report that Conlin, Lynn, and O’Donoghue (2003, 306) “interviewed customers leaving over 40 restaurants in Houston, Texas. The results indicate that people tend to view 15 percent of the bill as the appropriate tip for a server who performs well. As the bill size gets larger, however, meeting this social norm becomes more expensive. What Conlin, O’Donoghue, and Lynn’s data reveal is that, in

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fact, the percent-tip is a decreasing function of the bill size for both men and women and that men’s percent-tip is more responsive to the bill size than women’s.” Andreoni, Brown, and Rischall (2003, 128) write, “An important aspect of our results is that they provide direct evidence to support the growing feeling among fundraisers that men and women behave very differently with respect to charitable giving. Men are more sensitive to both price and income, for instance, and tend to concentrate their giving among fewer kinds of charities. And when the price of giving is low, men tend to give more to charity than women, but when the price is high the opposite is true.” Craig and others (2014) consider the effect of an increase in time cost on the return behavior of more than 900 blood donors in Australia, using both post-donation questionnaires and blood donations up to 3.5 years later. Exploiting the natural variation in time cost involved with donating blood, a 1-standard-deviation increase in the average wait time (an additional 20 minutes relative to the average wait time of about 45 minutes) would result in an 11% decrease in blood donations per year. For men, longer wait time is associated with less satisfaction from donating, lower intent to return, and longer delay before actually returning. While women also report less satisfaction and indicated they were less likely to return if they had to wait longer, longer wait times had no impact on the time until women returned to donate blood once more. That is, the return behavior of males is more elastic than that of females. Fisman, Jakiela, and Kariv (2014) study the external relevance of differences in distributive preferences on voting behavior. They conduct an incentivized experiment using the American Life Panel (ALP), with about 1000 participants dividing money between themselves and another (not-sampled) random ALP participant. Each participant makes about 50 decisions, in which both the budget as well as the price of giving was varied. One of these decisions was chosen for payment. They find that women are less likely to be efficiency oriented than men. About 750 of those participants also indicated for whom they voted in the 2012 presidential election. A binary indicator for efficiency-focused distributional preferences is negatively correlated with the likelihood of voting for Obama (in 2012), as well as belonging to the Democratic Party. In private communication, the authors note that the indicator for efficiency-focused preferences is larger than the coefficient for the female gender dummy, with females more likely to vote for Obama and to belong to the Democratic Party. IV.C Prisoner’s Dilemma and Public Good Games Rapoport and Chammah (1965), published in a psychology journal, is perhaps the earliest study of gender differences in incentivized prisoner’s dilemma games. They have pairs playing a 300-period repeated prisoner’s dilemma game.34 They find that male pairings exhibited the greatest rate of cooperation, followed by mixed pairings, with female pairings cooperating the least. Following this, there have been a number of papers considering gender differences in prisoner’s dilemma and public good games in the psychology literature. The literature on gender differences in public good and prisoner’s dilemma games in economics started later and was slower taking off than in psychology. For example, Ledyard (1995) surveys 6 papers on gender differences in public good games. He asks whether and how gender affects the rate of contribution. He concludes that, “I think the question remains open.” Eckel and Grossman, in their 2008b survey (with the most recent referenced paper published in 2001), included 8 public good games, concluding that, “In those settings where subjects are exposed to risk—i.e., public good

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experiments . . . —there is no significant evidence of systematic differences in the play of women and men.” The survey by Croson and Gneezy (2009) has 18 prisoner’s dilemma, social dilemma, and public good games with gender differences in behavior. Their summary is that “[a] large body of work identifies gender differences in other-regarding preferences. However, many of the results are contradictory. In some experiments, women are more altruistic, inequality averse, reciprocal, and cooperative than men, and in others they are less so. We believe that the cause of these conflicting results is that women are more sensitive to cues in the experimental context than men.” Balliet et al. (2011) published “Sex Differences in Cooperation: A Meta-Analytic Review of Social Dilemmas.” The studies they included had to have either adolescent or adult participants along with reporting participants gender. Further, “only studies using pure social dilemma paradigms were included (i.e. prisoner’s dilemma, public good, and resource dilemma). . . . We coded effect sizes for studies that either involved participants interacting with a confederate, a preprogrammed strategy, or another participant. Importantly, in all studies, participants believed they were interacting with other participants.” The latter makes it clear that these studies are not all published in economics journals. The meta-analysis contains 272 effect sizes. For each paper they use Cohen’s d-value as the measure of effect size, which is the difference in means divided by the pooled standard deviation.35 Table 8.2 shows the distribution of effect sizes for sex differences in cooperation in a stem-and-leaf plot for those studies that did not have null effects.36 To read this figure, note that Rapoport and Chammah (1965) is one of two studies with d = 0.57, that is, men cooperating significantly more than women. Balliet et al. (2011) conclude that the relationship between sex and cooperation in social dilemmas is not statistically different from zero.37 Further, when considering gender differences in cooperativeness based on the gender of one’s group members, they conclude that during mixed-sex interactions women were more cooperative than men, though during same-sex interaction, men were more cooperative than women, a result that is also borne out in pairwise interactions. One of Balliet et al.’s (2011) most intriguing results concerns what happens as interactions are repeated as opposed to one shot. They find that “men, compared to women tended to become more cooperative as iterations continued.” This result holds when excluding one-shot interactions, and indeed as the number of repeated interactions increases, men become significantly more cooperative compared to women. While there are obvious caveats with respect to meta-analyses, one that is particularly worrisome with respect to this result is the coding of repeated interactions. For example, Fudenberg, Rand, and Dreber (2012) conduct an infinitely repeated prisoner’s dilemma game with a continuation probability of 78 , meaning that the average length of the game is 8, with Balliet et al. recording this as 8 repetitions. Most recently, Gächter and Poen (2013) survey data from 17 papers on linear public good games with 6037 subjects in 274 sessions; all papers have Gächter as a coauthor and used similar parameters. In one-shot public good games they find that women gave 0.77 more than men (out of 20, with average contributions around 9). While the effect is significant, the difference is small. Iterated one-shot public good games—where subjects are randomly rematched after each round—reveal no gender differences in average contributions, though males are more likely to choose extreme contributions (0 or 20 out of 20). The lack of gender differences in one-shot public good games is confirmed when preferences for contribution are elicited by the strategy method (dependent on

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Chapter 8 TABLE 8.2: Stem-and-leaf diagram of the overall distribution of effect sizes for sex differences in cooperation. Source: Balliet et al. (2011). d-Value 1.5 1.4 1.3 1.2 1.1 1.0 0.9 0.8 0.7 0.6 0.5 0.4 0.3 0.2 0.1 0.0 −0.1 −0.2 −0.3 −0.4 −0.5 −0.6 −0.7 −0.8 −0.9 −1.0 −1.1 −1.2 −1.3 −1.4 −1.5

0.1 Units of the d-Value 3 0 48 8 06 00035578 0579 02334577 0077799 01355668 00023556666789 0011234566 0000223345556677778888899 000011223444556666799 0001111133346788 001124566677 0333566677 0012356677 0012358 2566 57 2448 4 7

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Notes: This plot omits three outliers: 1.65, −1.76, and −1.90. This plot includes only the 176 effect sizes that were coded and does not include the null effect studies that were estimated to have zero effect size.

the average contribution of others). Slightly more than 50% of subjects prefer to be conditional cooperators—that is, match the average contribution of the other players— and about 20% are perfect egoists—contribute zero—which is slightly more common among men than women (25% versus 18%). The remaining strategies are unclassified, though women give slightly less than man for large contributions of others, making up the lower fraction of participants who always donated nothing. Gächter and Poen also have data for women and men playing ten period repeated public good games with the same group members. While, on average, the contributions of women and men are not significantly different, men are slightly more responsive than women to the average contribution of others in the previous round. More importantly, men are much more strategic; their contributions decline more steeply than those of women over time and they contribute significantly less in the penultimate and

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the ultimate round. Contributions of men exhibit a positive correlation between how sensitive they are to contributions of others and how much they reduce their end-game contributions. Women, on the other hand, basically do not change their contribution over time, and there is no correlation between how sensitive they are to the contribution of others and how much they reduce their contributions over time. This higher level of strategic behavior by men can also be seen in how women and men react to punishment opportunities in the public good game. The standard result is that the opportunity to punish after a contribution round increases the donation to the public good in societies in which mostly free riders and not cooperators are punished, though no such increase is found in societies in which cooperators are heavily punished as well (Herrmann, Thöni, and Gächter 2008). Gächter and Poen (2013) find that in societies where mostly free riders are punished, men contribute significantly more to a public good with punishment than women do. No such difference is found in societies where cooperators are punished as well. To summarize, there do not seem to be large differences in average contributions in public good games between men and women. However, these similar average contributions may mask important strategic differences. More work is needed to robustly understand the extent to which women and men differ in their strategic behavior in cooperative games.38 It is worth noting, however, that just as in dictator games, male giving seems more dependent on the environment. Since there are no reliable gender differences in average behavior and the investigation of gender differences in strategic behavior has only began, I do not cover (and did not find many papers on) the external validity of gender differences or similarities in behavior in public good games or public good contributions, and volunteering, outside of the laboratory. For a paper that confirms the external relevance of behavior in public good games (though without addressing gender differences), see Rustagi, Engel, and Kosfeld (2010). IV.D New Directions The vast majority of papers on gender differences in altruism fall into a somewhat narrow band of games. It would be helpful to expand the set of games where altruism, or other regarding preferences, are studied. Vesterlund, Babcock, and Weingart (2014) have taken a step in that direction, addressing the question of whether women volunteer more often than men to perform nonpromotable tasks. This, in itself, may result in women falling behind in the workplace, being less likely to be promoted. Using data on volunteering for Senate committee duties at a large university corroborates the fact that women are more likely to perform such undesirable and undervalued duties. Looking at this relationship more closely, they conduct a laboratory experiment in which groups of 3 people are randomly rematched across rounds. Each person has to decide within a 2-minute interval whether to make an investment. There is no cost to delay, but if no one makes the investment, everyone receives $1. If at some point one player in the group makes the investment, the round ends, the investor receives $1.25, and the other 2 group members receive $2. Under mild assumptions there are three kinds of equilibria: a pure strategy asymmetric equilibrium where one individual invests, a symmetric mixedstrategy equilibrium where each player invests 23.3% of the time, and an asymmetric mixed-strategy equilibrium where one person does not invest and the other two invest 40% of the time. Data from 132 participants (72 males and 60 females) show that in about 82% of the rounds, the investment was made, and in roughly 63% of these it

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Probability of investing

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Figure 8.7: Probability of investing. Source: Vesterlund, Babcock, and Weingart (2014).

was made with 1 second or less to go. Figure 8.7 shows, for each round, the average investment rate by women and men when participants played in mixed-sex sessions (mixed_w and mixed_m, respectively). Women are significantly more likely to make the investment compared to men (35% compared to 21%). The distribution of investments by men is consistently lower than women across all 10 rounds. Gender differences in investment are only mildly attenuated when controlling for (gender differences in) risk, conformity, and other psychological variables (none of which are significant predictors of investment). To assess the extent to which the results are driven by inherent gender differences in preferences they repeat the experiment in single-sex groups. Figure 8.7 shows that the investment rates of women and men in single-sex groups are indistinguishable from one another (single_w and single_m, respectively). Women reduce and men increase their investment rate in single-sex compared to mixed groups. Note, however, that the overall chance that a group makes an investment is the same, whether in mixed-sex or in singlesex male or female groups. While the average rate of investment for men and women is essentially the same (occurring in 2.7 rounds on average), men are more likely to invest either seldom or very often, while women seem to be more concentrated around the “fair” investment rate of about one-third of the time. IV.E Conclusions Results for gender differences in altruism and cooperation are much more mixed than one might have expected. Considering average behavior, it seems that there are no reliable gender differences in average giving in the dictator game once the gender of the recipient is controlled for. In one-shot public good games, women are found to be slightly more cooperative than men. However, this result did not replicate when using a sequence of one-shot public good games (though men were found to be more likely to contribute extreme amounts—all or nothing). Likewise, repeated public good games show no significant gender differences in average contributions. However, both for dictator game giving as well as for repeated public good games, average similarities mask important differences. In dictator games, women are found to be less sensitive to the cost of giving (i.e., they are more equity than efficiency concerned compared to men). In finitely repeated public good games, men are found to be more strategic than women, especially in terms of adjusting their contributions downward as the end of

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the game approaches. More work is needed to understand the interplay between strategic sophistication, potential gender differences therein, and behavior in cooperative games. The literature on gender differences in altruism and cooperation has considered only a small spectrum of games and could benefit from breaking out of this confinement. A promising avenue is the work by Vesterlund, Babcock, and Weingart (2014), which combines preferences for contributions to a public good as well as concerns about discrimination and gender differences in beliefs about the behavior of others’.

V RISK After altruism and cooperation, the second strand of the literature on gender differences that has received an enormous amount of attention is risk attitudes. Since this topic attracted the attention of economists as well as psychologists, I’ll review the evidence in both. This literature, perhaps as much as the literature on gender differences in altruism, seems to potentially suffer not only from a publication bias, but also the fact that many people seem to have a clear idea of what the “correct” finding is. There are two main points and a piece of advice I want to convey in this section. The first point is that while gender differences in risk taking seem to exist, the evidence is far from persuasive that this gender difference is substantial in all environments. Because of the large heterogeneity in results, many surveys of the literature arrive at different conclusions and at times some reach much stronger conclusions than seem warranted by the evidence. The second point is that the heterogeneity in results of gender differences on risk preferences stems from the fact that under some elicitation techniques, gender differences in risk taking are very small (about 16% of a standard deviation; alternatively, assuming normal distributions of risk preferences, if a random man and a random woman are compared, there would be a 55% chance of being correct when saying that the more risk averse of the two is a woman). In fact, such an effect would often appear as a null result with sample sizes of a couple of hundred, as is common in many experiments. Other elicitation techniques yield somewhat larger gender differences, around 55% of a standard deviation (if a random man and a random woman are compared, there would be a 65% chance of being correct when saying that the more risk averse of the two is a woman). It is this variance in results that leads to very different conclusions when covering only a small fraction of the literature. This point really becomes evident when looking at the conclusions reached by various surveys of experimental studies in risk aversion. In principle, such heterogeneity in results is not so surprising given that risk itself does not seem to be a simple and stable factor. As a consequence, perhaps even more than for any other literature on gender differences, it will be important to show the extent to which (small) gender differences in the laboratory translate to externally relevant gender differences in observed behavior of economic interest, both in the lab and the field. Another reason for this special need stems from the enthusiastic adoption of (experimentally documented) gender differences in risk aversion as a plausible explanation for all kinds of gender differences in economic outcomes. I obviously applaud that economists embrace experimental results. However, experimental economists should be careful in their studies and conclusions and should not produce papers with biased results solely to pander to the taste of other economists. The goal of experimental economics should not be to produce evidence for any hypothesis.

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The main result of my survey of the literature on gender differences in risk aversion is that those differences do exist. However, there is substantial heterogeneity of that gender gap across situations and elicitation methods. The gender gap is very small, to the point of being almost nonexistent in some areas, though the gap is more pronounced in other environments. This leads my main advice. An experiment that investigates a hypothesis that could rely on gender differences in risk aversion should plan to implement a riskelicitation procedure that is germane to the question at hand. I will demonstrate this point using the last experiment I describe in this subsection, where I also elaborate on how to control for gender differences in risk aversion in experiments. There are several methodological issues when considering experiments on risk aversion. First is the question already addressed before: what is a good measure of risk aversion, and what are the correlations when using several measures? Such a debate has been present almost since the advent of studying risk aversion. An example is preference reversals by Lichtenstein and Slovic (1971). In a typical experiment, subjects are given the choice between a lottery with a high probability of winning a small amount (the P bet) or one with a small probability of winning a large amount of money (the $ bet). Subjects are also asked to state their willingness to sell each of these lotteries or state their certainty equivalent. The common finding is that subjects choose the P bet over the $ bet but have a higher selling price for the $ bet than the P bet. This robust preference reversal is, of course, not reconcilable with expected utility theory. In the last Handbook of Experimental Economics, Camerer (1995) described the already then very impressive bulk of evidence on different ways in which subjects deviate from expected utility. It is clearly problematic to map all those deviations back to a single measure of risk preferences and study gender differences in that measure. Perhaps as a result, the vast majority of the evidence on gender differences in risk aversion considers very simple choices over gambles that are not able to assess all the intricate ways in which behavior deviates from expected utility theory. Different gamble choices and different elicitation methods can capture different deviations from expected utility. They may, however, also result in differences in the extent to which there are gender differences in behavior. Section V.D addresses this concern and presents evidence that the extent of gender differences in risk aversion may strongly depend on the elicitation method. This suggests perhaps a more complex view than a simple summary that women are more risk averse than men. A further complication when studying risk aversion in the laboratory through small lotteries comes from what is now known as the Rabin critique (Rabin 2000). He posits that perhaps deviations from risk neutrality observed in low-stakes lab experiments should not be interpreted as risk aversion. This is because such risk aversion, if scaled to larger amounts, would lead to implausible choices. Despite that, I’ll keep using the term risk aversion to describe behavior observed with small-scale experiments. There has been only very little effort, so far, to assess changes in gender differences in risk aversion when changing the stakes; however, see Holt and Laury (2002) for a prominent exception. Another issue in studying risk aversion in the lab concerns how to pay participants if they make multiple decisions over lotteries and whether subjects should even make several choices or only one. Azrieli, Chambers, and Healy (2014) present a theoretical analysis of the issues that arise when subjects are given multiple decisions and in what instance choices in one decision may be distorted by choices in other decisions. They show that under mild assumptions, paying for one randomly chosen problem is essentially the only incentive-compatible mechanism. When the decisions by subjects

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are choices over lotteries and subjects are paid for one decision randomly with known probabilities, this generates a two-stage compound lottery. They claim that, “if we assume the reduction of compound lotteries, then the RPS [Random Problem Selection] mechanism is incentive compatible only if subjects are expected utility maximizers.” However, there is abundant evidence that subjects are not, in fact, expected utility maximizers.39 In terms of direct experimental evidence of the validity of the RPS mechanism, careful experimental comparisons do not reveal behavioral differences due to paying for one randomly chosen decision compared to paying for that same decision when subjects know in advance that only this decision is chosen for payment.40 Putting aside all the complications of studying (gender differences in) risk aversion, I will first cover early work and survey papers by psychologists. I then describe early economic papers and common elicitation methods in economics used to assess gender differences in risk aversion. I next discuss early economic surveys, followed by surveys using only a single elicitation method. I then discuss some recent results, and I close with an example and a discussion of how to design a risk elicitation method germane to the problem at hand. V.A Early Work and Surveys by Psychologists The very first experimental test on gender differences in risk aversion I could find is Swineford (1941). “A previous article [Swineford 1938] introduced a formula for measuring a personality trait by means of any objective test. The trait was defined as the tendency to gamble, and was found to be independent of the achievement score on the same test.” Specifically, subjects take a multiple-choice test. “The pupil is permitted to ask for credit of two, three, or four points for each question, with the understanding that twice the requested credit will be deducted from his score if the answer is wrong. It may be assumed that the pupil is gambling on his score against odds of two to one to the extent that he asks for extra credit for those items on which he is guessing. There being no way to separate the items guessed correctly from those representing correct knowledge, the gambling score must be based upon the incorrect items, all of which may be regarded as guesses. . . . The formula adopted to measure gambling, or G, was based on only the items marked ‘4,’ as follows: G = 100 × (Errors marked‘4 )/(Total errors + 12 omissions),” where omissions “are the items which were skipped within the test— not those omitted at the end of the test for lack of time.”41 The paper provides outcomes of 344 students taking each of 4 tests.42 The result is that “(1) Boys have a significantly greater tendency to gamble on their test scores than do girls, particularly on an unfamiliar type of test. (2) Both boys and girls have a significantly greater tendency to gamble on unfamiliar material than on familiar material. (4) . . . the G scores are independent of the scores on the tests from which they were computed” (pp. 443–44). One reason to describe this paper, apart from its being the first, is that the last paper discussed in this section provides a nice example of a modern look at gender differences in test taking. Specifically, the paper disentangles the extent to which gender differences in test taking may be due to gender differences in risk aversion or gender differences in other domains such as test scores or beliefs about the chances the question was answered correctly. The first paper I found that uses incentivized choices over lotteries to study gender differences toward risk is Kass (1964, 579). He has 52 children aged 6 to 10 choosing between 3 slot machines.43 The payoffs of each machine were illustrated by pulling the lever on each machine 5 consecutive times (the returns were not described).

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Each slot machine had an expected return of 0, one gave a penny back for each penny put in, one gave 3 pennies back with probability 1/3 (in fact: “On the 1/3 machine S[ubject] won three pennies at a time, dispensed once in random position, within a block of three trials,” and the last gave 8 pennies back with probability 1/8.44 In the experiment the “S[ubject] was stopped after 210 trials. At this time S was told he could now play only the machine he liked best and could not play the other two. S’s preference was recorded, and he was then told that he could choose the prize he wanted to buy with his pennies.” The first result concerns the last 30 trials before this forced choice, where a response is a choice to put money in a slot machine: “boys made the greatest number of responses on the machines with the intermediate and low probabilities of payoff and the least number of responses on the high probability machine. For the girls, the opposite effect is apparent.” The difference is significant. “At the end of the experimental session, each S was told to pick the machine he liked best and to play only that one. On these forced choice trials, 61.1 per cent of the boys and 38.0 per cent of the girls did not pick the machine they had played most frequently during the previous 30 trials.” There is no more discussion about possible gender differences in those choices. Indeed, the summary conclusion suggests that only in the free-choice part were there any gender differences in choices.45 Therefore, the first paper with incentivized choices over lotteries reports two effects, one with a gender difference in choices, and one where there is no gender difference. However, both of those previous papers are seen as evidence of gender differences in risk aversion. For example, the second-oldest paper of which I am aware that uses incentivized gambles, Slovic (1966, 170), announces that, “At present, evidence indicating that boys are willing to take greater risks than girls is scarce.” The exceptions are the two papers described earlier.46 A first summary of the experimental literature on gender differences in risk aversion is from psychologists. Byrnes, Miller, and Schafer (1999) conduct a meta-analysis of 150 studies comparing the risk taking behavior of women and men.47 They have a total of 322 effects. The mean of Cohen’s d (weighted by the inverse of each d’s variance) was found to be d = 0.13, with a 95% confidence interval of 0.12 to 0.14.48 Assuming normal distributions, a Cohen’s d of 0.13 implies that when comparing a random man to a random woman, there is a 54% chance that the woman is more risk averse.49 The paper states that “nearly half (48%) [the effects] were larger than .20 (the conventional cutoff point for small effects).” Byrnes, Miller, and Schafer (1999, 378) conclude that while the overall mean effect size of d = 0.13 would be labeled as small in some statistical circles, such differences should still be “a matter of concern,” since small differences can accumulate across behaviors and time to produce substantial gender differences in various outcomes, such as driving injuries or deaths. To see that in psychology the study of gender differences in risk aversion has been a growing field, note that in the first 17 years covered by the study (1964–80) there were 83 effects, compared to 235 effects in papers published from 1981 to 1997.50 The mean and confidence interval for these two periods were d = 0.20 (0.17 to .23) and d = 0.13 (0.12 to 0.14), so, “the gender gap seems to be growing smaller over time” (Byrnes, Miller, and Schafer 1999, 366). It is not clear that such a conclusion is really related to changes in how women behave differently from men compared to a conclusion about changes in the discipline. While publication date is the obvious difference between those two sets of papers, it could, of course, also be that different risk-elicitation methods became more or less fashionable over time, and different elicitation methods may yield different gender

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Distribution of Cohen’s d 1.2 1 0.8 0.6 0.4 0.2 0 –0.2 –0.4 –0.6 –0.8 –1

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Figure 8.8: Distribution of the 35 effects sizes (women more risk averse than men) from 17 papers that use incentivized gambles and are analyzed by Byrnes, Miller, and Schafer (1999).

differences in risk aversion. Interestingly, the papers in top-tier journals (containing 14 studies) have the lowest effect size, d = 0.03 (0.01 to 0.05). Many of the 150 papers analyzed in Byrnes, Miller, and Schafer (1999, 370) are from psychology. In fact, not a single one was published in an economics journal, and in only 48 were “participants observed by researchers as they engaged in various activities that were judged by the researchers to have some degree of risk (e.g. making a left turn in front of traffic).” Of those, the total Cohen’s d was d = 0.19 (95% confidence interval 0.16 to 0.22). Of those 48 papers (and dissertations), only 17 use “gambling tasks” (see their Table 1).51 While I counted 17 papers with 35 effects from their Table 1, Byrnes, Miller, and Schafer (1999) report that the mean effect size for the 33 effects in the gambling task is 0.21 (95% confidence interval of 0.14 to 0.28; see Table 2 on page 377.) They then divide those effects by age of participants and find d = 0.03 for children aged 9 and younger, d = 0.27 for children aged 10 to 13 as well as those aged 14 to 17, and d = 0.31 for college students. The total distribution of the 35 effects I counted can be seen in Figure 8.8. Note, however, that the Kass (1964) study described earlier is coded as d = 0.80. While this represents the choices in the last 30 trials before the forced choice, it also suggests that the (presumable) lack of a gender gap in the forced choice part of the experiment is not represented.52 So, while there seems to be a gender difference in risk aversion, about 20% of the effects show men to be more risk averse than women, and only about 50% of the studies have an effect size bigger than 0.2, what is often considered the cutoff for a small effect. Recall that, assuming normal distributions, a Cohen’s d of 0.2 still implies only a 56% chance that a random man is less risk averse than a random woman. Analogously, about 600 subjects would be needed to get a significant gender effect at 10%, assuming a power level of 0.8. This first summary of the psychology literature already suggests a very moderate message: While gender differences in risk taking exist and women are more risk averse than men, those differences are small. In fact many studies with sample sizes of a few hundred will not find significant gender differences. Furthermore, because the effect is small, gender differences in risk aversion will probably not account for gender differences in many experimental findings or for large differences in many economic decisions.

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Chapter 8 TABLE 8.3: The ten paired lottery-choice decisions with low payoffs. Source: Holt and Laury (2002). Option A 1 10 2 10 3 10 4 10 5 10 6 10 7 10 8 10 9 10 10 10

of $2.00, of $2.00, of $2.00, of $2.00, of $2.00, of $2.00, of $2.00, of $2.00, of $2.00, of $2.00,

Option B 9 10 8 10 7 10 6 10 5 10 4 10 3 10 2 10 1 10 0 10

of $1.60 of $1.60 of $1.60 of $1.60 of $1.60 of $1.60 of $1.60 of $1.60 of $1.60 of $1.60

1 10 2 10 3 10 4 10 5 10 6 10 7 10 8 10 9 10 10 10

of $3.85, of $3.85, of $3.85, of $3.85, of $3.85, of $3.85, of $3.85, of $3.85, of $3.85, of $3.85,

9 10 8 10 7 10 6 10 5 10 4 10 3 10 2 10 1 10 0 10

Expected Payoff Difference

of $0.10

$1.17

of $0.10

$0.83

of $0.10

$0.50

of $0.10

$0.16

of $0.10

−$0.18

of $0.10

−$0.51

of $0.10

−$0.85

of $0.10

−$1.18

of $0.10

−$1.52

of $0.10

−$1.85

V.B Early and Most Commonly Used Elicitation Methods in Economics The oldest published paper in economics on gender differences in risk aversion that I found is by Schubert et al. (1999, 382) in American Economic Review Papers and Proceedings. In their experiments 76 men and 65 women provide certainty equivalents for four gambles. “Payoffs in Swiss francs (1 SFr = $ 0.60) and their probabilities were (30 SFr, 1/6; 10 SFr, 5/6), (30 SFr, 1/2; 10 SFr, 1/2), (30 SFr, 5/6; 10 SFr, 1/6) and (50 SFr, 1/2; 20 SFr, 1/2), respectively.” Subjects were either in a “context” treatment, in which case they first made four decisions in an investment/gain frame and then the same four in an insurance/loss frame (where losses were relative to an initial endowment). In the “abstract” treatment, participants made the same choices, though choices were now framed as abstract gambling decisions. While there are no gender differences in the context treatment, in the abstract gambling treatment, women are more risk averse in the gain domain—their certainty equivalent is almost lower by 1—but more risk seeking in the loss domain where the female certainty equivalent is higher by 1.3, when controlling for disposable income per month in thousands of Swiss francs. This first paper suggests that economic style experiments may lead to a similar conclusion than psychology experiments. Small samples may often not find gender differences in risk aversion, which suggests that gender differences in risk aversion, even if they exist, are probably rather small. This is only the beginning of a large literature in experimental economics on measuring risk aversion and checking for gender differences therein. While many different methods have been used to study gender differences in risk aversion, two stand out in their adoption by other researchers. Probably the most popular method is by Holt and Laury (2002). They had students make a series of binary choices between two lotteries, option A or option B, where the variance of option A is lower. In each row, the set of possible outcomes of option A (and B, respectively) are held constant; what varies is only the probability of receiving the higher outcome. The choices are presented in Table 8.3 (where subjects, however, did not see the third column that computed the expected payoff difference between option A and option B). A risk-neutral subject would choose option A in the first 4 choices and

Probability of A

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531

1 0.9 0.8 0.7 0.6 0.5 0.4 0.3 0.2 0.1 0 1

2

3

4

5 6 Decision

7

8

9

10

Figure 8.9: Proportion of safe choices in each decision: data averages and predictions. Source: Holt and Laury (2002). Data averages for low real payoffs [solid line with dots], 20 times real [squares], 50 times real [diamonds], 90 times real [triangles], and riskneutral prediction [dashed line].

then option B thereafter. A risk-averse person may switch to option B only later, as the probability of the best outcome increases, though everyone should choose option B in their last choice. The standard Holt-Laury task is to give subjects those 10 choices (or sometimes fewer, eliminating the final rows). Then one row is randomly chosen, and subjects are paid the outcome of their chosen lottery in that row. In their baseline treatment, Holt and Laury (2002) have subjects first make choices for each line in Table 8.3, with the understanding that one of those choices would be paid. In round 2, subjects made the same choices again, with hypothetical payoffs at 20 times the level of Table 8.3. In the third round, subjects once more choose with payoffs 20 times higher than the payoff in round one, with one round chosen for payment. “To control for wealth effects between the high and low real-payoff treatments, subjects were required to give up what they had earned in the first low-payoff task in order to participate in the high-payoff decision. . . . Nobody declined to participate so there is no selection bias.” (Holt and Laury 2002, 1646). In the final round 4, subjects made real choices once more with the initial low payoffs from Table 8.3; 93 subjects made those four choices, while 25 subjects had rounds 1, 2, and 4 only and 57 had rounds 1, 3, and 4 only. Finally, 19 subjects had a treatment where, instead of multiplying payoffs by 20, they were multiplied by 50 in rounds 2 and 3, and a final 18 subjects had payoffs in rounds 2 and 3 multiplied by 90. The choices of subjects are summarized in the Figure 8.9, which clearly shows that as stakes increase, subjects become more risk averse. At the end of their Section II, Holt and Laury (2002, 1651 have the following sentences. “Using any of the real-payoff decisions to measure risk aversion, income has a mildly negative effect on risk aversion ( p < 0.06). Other variables (major, MBA, faculty, age, etc.) were not significant. Using low-payoff decisions only, we find that men are slightly less risk averse ( p < 0.05), making about 0.5 fewer safe choices . . . The surprising result for our data is that this gender effect disappears in the three highpayoff treatments.”

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Chapter 8 TABLE 8.4: Five options of the Eckel-Grossman task. Source: Eckel and Grossman (2002). Option

Event

Probability

Outcome

1

A B

50 50

16 16

2

A B

50 50

24 12

3

A B

50 50

32 8

4

A B

50 50

40 40

5

A B

50 50

48 0

TABLE 8.5: The choices of women and men in Eckel and Grossman (2002). Choices

Men

Women

1 2 3 4 5

2 17 25 24 36

8 18 40 17 13

Average

3.72

3.10

A second common way to assess gender differences in risk aversion is what became known as the Eckel-Grossman (EG) task and was used by Eckel and Grossman (2002). It is based on a method originally used by Binswanger (1980). Eckel and Grossman study gender differences in choices over lotteries as well as gender differences in beliefs about each other’s risk behavior. Subjects were shown a sheet with five possible gambles and choose one (Table 8.4).53 One option is a riskless sure payoff, and the other options are 50:50 gambles where both the variance and the mean in payoffs increase. “Comparing men’s and women’s gamble choices, we found that women were significantly more risk averse than men. For example, less than 2% of the men, but over 8% of the women, chose the least risky gamble, whereas over one-third of the men, but only 13% of the women, selected the riskiest gamble. The median gamble choice was 4 and 3 for men and women, respectively. Men’s mean gamble choice was 3.72 (95% confidence intervals: 3.49–3.95) versus 3.10 (2.87–3.33) for women, a significant difference [t(198) = 3.83, P < .001]” (Eckel and Grossman 2002, 287). For the distribution of male and female choices see Table 8.5. To summarize, in the very first experimental study by Schubert et al. (1999), with a total of 4 effects (or treatments), women were found to be more risk averse in one, more risk seeking in one, and not significantly different from men in two treatments. However, in the environment that received the most attention by experimental economists, abstract gambles in the gains domain, women were found to be more risk averse than men. Of the two most common risk-elicitation methods used to study gender differences in risk aversion, Holt and Laury (2002) found women to be more risk

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averse than men when stakes were around a few dollars. However, there were no gender differences in risk aversion in the three treatments where payoffs were around $10 or more. Finally, Eckel and Grossman (2002) found gender differences in risk aversion with their elicitation method. V.C Early Economic Surveys There are two (early) surveys in experimental economics on gender differences in risk aversion; Eckel and Grossman (2008c), which seems to have been written quite a bit earlier, and Croson and Gneezy (2009). These two surveys, as well as the survey by Byrnes, Miller, and Schafer (1999) described earlier, all reach the same overall conclusion, namely, that women are more risk averse than men. However this overall message is delivered with quite different forcefulness. The most moderate is perhaps Byrnes, Miller, and Shafer, who write that “the majority (i.e., 60%) of the effects support the idea of greater risk taking on the part of males.” In fact, nearly half the studies (48%) had Cohen’s d effect sizes larger than 0.2 (the conventional cutoff point for small effects). However, in a sizable minority (i.e., 40%) the effect size was either negative— that is, males were found to be more risk averse than females—or close to zero. Eckel and Grossman (2008c), in their conclusions, write: “The findings from field studies conclude that women are more risk averse than men. The findings of laboratory experiments are, however, somewhat less conclusive. While the preponderance of laboratory evidence is consistent with field evidence, there is enough counter-evidence to warrant caution.” This message is somewhat less moderate in their introduction: “In most studies, women are found to be more averse to risk than men. Studies with contextual frames show less consistent results.” And the strongest conclusions are reached by (Croson and Gneezy 2009, 449): “The robust finding is that men are more risk-prone than are women.” While Byrnes, Miller, and Schafer (1999) suggested that “the gender gap seems to be growing smaller over time,” the opposite seems to have happened in the experimental economics literature. However, it could also be that different authors interpret the existing evidence differently. For example, Croson and Gneezy (2009, 449), summarizing Eckel and Grosman (2008c) and Byrnes, Miller, and Schafer (1999), write that, “Previous surveys of economics report the same conclusions: women are more risk averse than men in the vast majority of environments and tasks.” To address whether the findings on gender differences in risk aversion have changed in the experimental economics literature, Table 8.6 considers the papers summarized by each survey, focusing on experiments using objective lotteries. Eckel and Grossman (2008c) review 14 papers and seem to have aimed to provide a review of the existing literature at the time of writing the survey, which was before 2008 (see their Table 1 in the paper, which, however, fails to include one paper I take the liberty to add in the Table 8.6).54 Croson and Gneezy (2009) review 10 papers in their survey (see their Table 1) without providing any obvious selection criterion. They have two papers by Eckel and Grossman published in 2008, though the two references refer to the two survey chapters in the Handbook of Experimental Economics Results (one on risk and one on altruism and cooperation, cited here as Eckel and Grossman (2008c, 2008b), respectively). I will treat the two as Eckel and Grossman, 2008. Croson and Gneezy also mention an eleventh study in a footnote, which they dismiss.55 Table 8.6 shows for each paper covered in either Eckel and Grossman (2008c) or Croson and Gneezy (2009) whether only one of them or both surveyed it, as well as which, if any, gender was

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Chapter 8 TABLE 8.6: Experiments on objective lotteries surveyed by Eckel and Grossman and Croson and Gneezy. More Risk Averse

Women Moore and Eckel (2003) Brinig (1995) Levy et al. (1999)

Neither Moore and Eckel (2003)

Eckel and Grossman only

Schubert et al. (2000) Gysler et al. (2002) Harbaugh et al. (2002) Kruse and Thompson (2003) Harrison et al. (2005)

Schubert et al. (1999) Eckel and Grossman Holt and Laury (2002) as well as Levin et al. (1988) Croson and Gneezy Powell and Ansic (1997) Hartog et al. (2002) Eckel and Grossman (2008a)

Schubert et al. (1999) Holt and Laury (2002)

Croson and Gneezy Only

Men Moore and Eckel 2003

Schubert et al. (1999)

Finucane et al. (2000) Dohmen et al. (2005) Fehr-Duda et al. (2006)

found to be more risk averse. Some papers have multiple results and hence are in several columns. The papers are ordered such that papers with multiple but different effects are listed first; otherwise, papers are listed in order of the year they were published (be it working paper or publication). Excluding papers that find both evidence of no gender differences and of women being more risk averse, Eckel and Grossman (2008c) cite 6 papers that found women to be more risk averse and 5 that found no gender differences. It is easy to see how they reached the conclusion that while there is evidence that women are more risk averse than men, there is enough counterevidence to warrant caution. Table 8.6 also makes it clear why Croson and Gneezy (2009) reached a much stronger conclusion. Apart from Schubert et al. (1999)—the first experimental economics paper on gender differences in risk aversion in a top economics journal—and Holt and Laury (2002), all the papers they surveyed found women to be more risk averse than men.56 One reason different surveys reach different conclusions is the heterogeneity of experimental results. This could have two potential reasons. First, it could be that there is a wide range of results because risk preferences are very malleable and subject to framing. It could also be that gender differences in risk aversion, while perhaps statistically significant, are economically small, so that samples of several hundred do not yield reliable results. In that case the existing pattern of published papers would suggest a publication bias favoring papers in which women are more risk averse and penalizing papers that find men to be more risk averse. A second possible explanation for the heterogeneity of experimental results is that different elicitation methods measure different aspects of risk preferences and the gender gap in risk preferences is dependent on the specific way in which attitudes toward risk are measured. Different explanations suggest different advice concerning control treatments designed to assess the role of risk aversion in the main result of any given experiment. If gender differences in risk preferences are economically small but the results are

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sufficiently noisy that small samples may not reflect the general finding, then experiments should assess the risk preferences of their sample rather than assuming specific risk distributions. If gender differences in risk depend on the specific risk measure, then each experiment that attributes some portion of gender differences in a given task to gender differences in risk aversion should be careful to choose an elicitation method germane to the task at hand. One way to address which of the two possible explanations is more responsible for the variety of results is to assess the extent of gender differences in risk attitudes using a single experimental method and capturing all (or at least many) papers that use that method. This point has been made both by Eckel and Grossman (2008c) and Byrnes, Miller, and Schafer (1999). V.D Recent Economic Surveys and Meta-Analyses on Specific Elicitation Tasks The first paper in economics of which I’m aware that summarizes risk-preference experiments employing the same method involves a new task to measure risk aversion. It was originally developed by Gneezy and Potters (1997) to assess whether there are differences in risk aversion due to framing.57 In their investment game, agents receive a fixed amount of money, $X, and can decide to invest any part x of X in an investment. The investment yields dividends of kx with probability p and nothing otherwise. The several papers using this game were designed to study questions different from gender differences in investment behavior. Charness and Gneezy (2012) summarize a series of papers that use the Gneezy and Potters (1997) investment game, where the values of k and p are such that pk >1, meaning a risk-neutral agent would invest everything, that is, x = X. Charness and Gneezy (2012) “report data from all studies (of which we are aware) using this method for testing risk aversion,” which turns out to be 14. They find that in all but one study, women invest less than men. This leads to the following summary statement (made in their introduction): “The striking and consistent result is that despite the large environmental differences among the sets of experiments, a consistent gender difference is reported: Men choose a higher x than women do.”58 The second recent survey of which I am aware that focuses on a specific elicitation method is Filippin and Crosetto (2014). They note that while many papers replicate the Holt and Laury (HL; 2002) task, not all of them report gender effects. They set out to do a meta-analysis of published results and tried to get the data from all these papers to present a unified analysis. They ended up with the data from 63 papers for a total of 8713 subjects.59 To ensure comparability across papers, they code the number of safe choices as the last probability of the high outcome at which option A, the gamble with lower variance, was chosen over option B, the gamble with the higher variance (recall Table 8.3 from Section V.B).60 In a first analysis, they provide, for each paper for which they have detailed data (54), statistics of subjects who made consistent choices (i.e., switched once and did not make dominated choices).61 Filippin and Crosetto (2014, 12) compute “the mean number of safe choices by gender, as well as the results of a non-parametric Mann-Whitney test.” In 40 papers women are found to be more risk averse, in 7 of which differences are significant at a 5% level. For the remaining 14 papers, men are found to be more risk averse, though not significantly so. Such a mixed message, leaning toward a finding that there are either no gender differences or that women are more risk averse but not by much, is also found when considering Cohen’s d for each paper. A total of 3 papers find

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Chapter 8 TABLE 8.7: Summary statistics of safe choices of consistent subjects. Mean

St. Dev.

N

Whole Sample Males Females

5.63 5.47 5.78

1.91 1.89 1.91

5,935 2,998 2,937

Microdata Males Females

5.73 5.59 5.87

1.96 1.94 1.97

4,324 2,119 2,205

Notes: Data from papers using the Holt-Laury method that report: Microdata: Every binary choice of all subjects, Whole sample: The number of safe choices as well as whether the subject made consistent choices. Source: Filippin and Crosetto (2014).

a medium effect (d of 0.5 to 0.8), 23 find a small effect (d of 0.2 to 0.5), and 22 find a null effect (d less than 0.2, in both directions, i.e., women or men being more risk averse). At the same time 5 papers find a small effect, and 1 paper finds a medium effect in the opposite direction (i.e., males are more risk averse than females). Filippin and Crosetto (2014) then merge the data sets. “Microdata” consists of all data sets that include every binary choice of participants, while “whole sample” includes data sets that report only the number of safe options a subject chose and whether the subject made consistent choices. Table 8.7 shows the mean number of safe choices for both women and men, as well as the standard deviation. On average, males seek more risk (make fewer safe choices), significantly so in both samples, though the variance is similar. “The Cohen’s d on the pooled sample is d = 0.163, a tiny 16% of a standard deviation, even below the threshold of 0.2 used to identify a small effect. To give an example of how small this is, consider that if we compare two random persons, and assume normal distribution of risk preferences, we would have a [55]% chance of being correct when saying that the more risk averse of the two is a woman, against a 50% rate if we just randomized our answer” (Filippin and Crosetto 2014, 18). Put differently, the minimum sample size to get a 5% significant result using a two-tailed t-test study with statistical power level of 0.8 would be about 600 subjects per gender. Filippin and Crosetto (2014) also discuss other elicitation methods. They report that the sizable gender gap in choices observed by Eckel and Grossman (2002) in the Eckel-Grossman (EG) task also appears in replications of this task. They cite 6 papers coauthored by Catherine Eckel, as well as by Crosetto and Filippin (2013b) and Wik and others (2004). Buser, Niederle, and Oosterbeek (2014), described in Section II, administer an EG task to almost four hundred 15-year-old Dutch school children and also find significant gender differences in risk taking. The only paper Filippin and Crosetto (2014) are aware of that does not find significant gender differences is Cleave et al. (2010). While they replicate the gender gap in a wide sample, a specific subsample of subjects who also participated in later experiments does not find that women are more risk averse. Filippin and Crosetto (2014) then provide a Cohen’s d both for the investment game from Gneezy and Potters (1997) and the Eckel-Grossman (EG) task from Eckel and Grossman (2002).62 The average effect size coincides for the two elicitation methods, and it is equal to d = 0.55, with women being more risk averse than men. To compare

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the effect size of the EG task (and the investment game) vis-à-vis the HL task, note that the effect size is more than three times as high in the EG than in the HL task. This means if we were to compare two random persons and assume normal distribution of risk preferences, we would have a 65% chance of being correct when saying that the more risk averse of the two is a woman in the EG task, against a 55% rate in the HL task. Put differently, the minimum sample size to get a 5% significant result using a two-tailed t-test study with statistical power level of 0.8 in the EG task would be about 55 subjects per gender compared to 600 in the HL task. Filippin and Crosetto (2014, 22) speculate as to what determines the extent to which women are more risk averse than men. They say that it has been argued that HL is more difficult to understand than other methods, making differences harder to detect (e.g., Dave et al. 2010). However, “[t]he SNR [signal-to-noise ratio (mean/standard deviation)] in our dataset of HL replications is equal to 3.34, higher than the average of the replications of the SNR of the Investment Game [of Gneezy-Potters] (2.06) and the EG [Eckel-Grossman] task (2.41).” Given that differences between methods do not seem to stem from a different precision in measuring risk attitudes, Filippin and Crosetto (2014) offer three dimensions that differ between the Holt-Laury task on the one hand and the Investment Game and the Eckel-Grossman task on the other hand: 1. Is the menu of lotteries generated by • •

Changes in probabilities (HL) Changes in outcomes (EG and investment game)?

2. What domains of risk preferences are considered? HL measures preferences both in the risk-averse and risk-loving domain, while other methods do not. 3. Is there a safe option available? A safe option is present both in the Investment Game and EG task, but not in the HL task. First results of Filippin and Crosetto (2014) indicate that while adding a safe option to HL increases the gender gap in choices, removing it from EG does not seem to reduce the gender gap. To summarize, the message from the experimental literature is complex. While the overall evidence points to women being more risk averse than men, there is large heterogeneity in the extent of this gender gap. The Holt-Laury task, which is the experimental method that Filippin and Crosetto (2014) found the most papers employing, generates a gender gap in risk aversion small enough that experiments using several hundreds of subjects will, in general, not find significant gender differences. On the other hand, elicitation methods such as the Eckel-Grossman task or the investment game generate a larger gap in risk aversion, 0.55 of a standard deviation. However, in psychology this is considered a medium effect that can be achieved quite reliably with just over 100 subjects. Clearly, understanding when gender differences in risk aversion are present and when they are rather small to almost non-existent remains an open question. The heterogeneity in results suggests that any given experiment should not presume a specific distribution of risk preferences. Rather, an experiment that aims to assess the impact of risk aversion on the main result should aim to generate a risk measure of the kinds of risk subjects are exposed to in the experiment. That is, the risk measure may have to be very germane to the task at hand.

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V.E Stability of Risk Preferences and Their External Relevance The heterogeneity of results on gender differences in attitudes toward risk suggests a concern whether elicited risk preferences are a reliable measure of a subject’s risk attitude. Put differently, to what extent is there a stable risk preference, and which elicitation method comes closest to capturing it? And, more importantly, is there a risk measure that captures sufficiently broad risk attitudes and reliably correlates with behavior we expect to depend on the subjects’ risk preferences? While the first question concerns internal validity, the second concerns external validity, both of which are important. Eventually, however, the question is whether gender differences in risk attitudes have external relevance. That is, do experimental risk measures correlate with economically relevant behavior or outcomes? Furthermore, given the focus of this chapter, can gender differences in the experimental risk measure account for gender differences observed in economic behavior or outcomes? I start by describing three ways in which we can assess the external validity of risk measures. These can also be seen as three hurdles to using experimentally elicited risk measures to predict choices outside the lab. The first way, or hurdle, concerns the stability of risk preferences across elicitation methods but within a domain or, more precisely, for the same lottery choices. Second, is there stability in risk preferences across domains? For example, will risk preferences measured using the EG task correlate with those using the HL task? Or, will risk preferences measured in, say, choices over different car insurances match those of choices over different homeowner or health insurances? Finally, is there stability of risk preferences using the same elicitation method and the same domain? That is, if we ask participants at two separate times the same questions in the same ways, how correlated will their choices be? For each of those three ways to assess external validity of risk measurements, I’ll mention a few relevant papers covering early work and some covering more current work. I will then discuss work relating risk preferences to choices outside the lab, focusing on work that uses risk measures to account for gender differences in economic outcomes (given the focus of this chapter). V.E.1 THE STABILITY OF RISK PREFERENCES A first problem when considering the external relevance of experimentally elicited risk preferences is the considerable heterogeneity of results across elicitation methods even for the same decisions over uncertain outcomes. For economic-style experiments that show that the same individual may have different risk attitudes, depending on the elicitation method, see Slovic (1972).63 The paper uses the two elicitation methods from the preference-reversal literature (see Lichtenstein and Slovic 1971). Specifically, subjects chose between a lottery with a high probability of winning a small amount (the 6 chance to lose 230 points— P-bet)—for example, 30/36 chance to win 250 points and 36 or one with a small probability of winning a large amount of money (the $-bet)—for 9 chance to win 980 points and 27 chance to lose 100 points. Subjects are example, 36 36 also asked to state their willingness to sell each of these lotteries or state their certainty equivalent. The common finding is that subjects choose the P-bet over the $-bet but have a higher selling price for the $-bet than the P-bet. Some economists have been intrigued, but skeptical, of this result. Grether and Plott (1979, 634) replicated the preference reversal result and state: “Needless to say the results we obtained were not those expected when we initiated this study. Our design controlled for all the economictheoretic explanations of the phenomenon which we could find. The preference reversal phenomenon which is inconsistent with the traditional statement of preference theory remains.”

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539

600

Mean difference in selling price $ BET minus P BET

500

400

300

200

100

–3.0

–1.5

+1.0

–100

+2.0

+3.0

Mean preference for the $ BET – choice index

Figure 8.10: Relationship between choice and selling-price indexes across the total sample of subjects (r = 0.46). Source: Slovic (1972).

Slovic (1972) asks whether the two methods result not only in a different magnitude of estimated risk preferences, but also in a different ordering of which subjects are more risk averse than others. Specifically, when subjects choose between lotteries, they indicated whether the preference was from (1) “slight” to (4) “very strong.” In Figure 8.10 each subject is represented as a point, where the x-coordinate is the mean preference for the $-bet using the augmented choice index, and the y-coordinate is the mean difference in selling price between the $-bet and the P-bet. Figure 8.10 confirms the preference reversal: While the preference of the $-bet using the choice index is negative in general, most subjects have a higher selling price for the $-bet than the P-bet. The correlation between these two measures 0.46. This correlation is similar for women and men, separately (0.4 and 0.55, respectively). Slovic (1972, 133) concludes: “The fact that a simple change in response mode can create so much inconsistency among individuals’ relative standings in the group implies that high correlations between risk-taking measures in structurally different settings and other behaviors are unlikely to be found.” Very similar results have been obtained more recently by Harbaugh, Krause, and Vesterlund (2010). A second issue in determining the external relevance of experimentally elicited risk preferences is whether people even have a unique risk attitude or risk parameter

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that guides all their decisions. That is, what is the variance across different elicitation methods or across different domains, such as attitudes toward risk in a health or a car insurance domain? Given that gender differences in risk aversion depend on the elicitation method, it is clear that even rankings of ordinal risk attitudes may be different across measurements when the sample contains both women and men. The problem could, however, also arise within gender. Slovic (1962, 69) presents one of the first investigations on the correlation of 9 different hypothetical risk measures (8 of which can be ordered) that have been previously used by psychologists (see also Slovic 1964).64 “The results show that only 5 correlations out of 28 reach significance in the predicted direction and none of these correlations exceed 0.34. Another 10 of these correlations are negative, 2 significantly so.” The paper concludes that “[t]he implications of the present study for the existence and measurement of a general risk taking trait are (a) none or only a few of the variables analyzed actually measure the trait; or (b) willingness to take risks may not be a general trait at all but rather one which varies from situation to situation within the same individual” (p. 70).65 Blais and Weber (2006, 36) propose a “domain-specific risk-taking (DOSPERT)” scale for adult populations; see also Weber, Blais, and Betz (2002). “The risk-taking scale of the 30-item version of the revised DOSPERT Scale evaluates behavioral intentions, that is, the likelihood with which respondents might engage in risky behaviors originating from five domains of life (ethical, financial, health/safety, social, and recreational risks) using a 7-point rating scale ranging from 1 (Extremely Unlikely) to 7 (Extremely Likely). Sample items include ‘Having an affair with a married man/woman’ (Ethical), ‘Investing 10% of your annual income in a new business venture’ (Financial), ‘Engaging in unprotected sex’ (Health/Safety), ‘Disagreeing with an authority figure on a major issue’ (Social), and ‘Taking a weekend sky-diving class’ (Recreational).” Blais and Weber find that the degree of risk taking was highly domain specific and that subjects were not consistently risk averse or risk seeking across all 5 domains. However, women were found to be more risk averse in all domains apart from social risk. Blais and Weber also ask about the perceived benefits and the perceived risks of an action. “The risk-perception scale evaluates the respondents’ gut level assessment of how risky each behavior is on a 7-point rating scale ranging from 1 (Not at all) to 7 (Extremely Risky).” These have a large influence on risk taking. “A regression of risk taking . . . on expected benefits and perceived risks suggests that gender and content domain differences in apparent risk taking are associated with differences in the perception of the activities’ benefits and risk, rather than with differences in attitude towards perceived risk.” The importance of perceptions of risk is often neglected in economics inquiries where we prefer to control for the risk at hand. See Erev and Haruvy (Chapter 10) and Erev and Roth (2014) for a discussion on how focusing on objective risk may provide a distorted view of the importance of various biases in decision making. A hypothetical risk question that is more common in economics is the one used by the German Socio Economic Panel (SOEP), a representative sample of the adult population living in Germany. In one of their waves they introduced the following risk question: “How do you see yourself: are you generally a person who is fully prepared to take risks or do you try to avoid taking risks? Please tick the box on the scale, where the value 0 means: ‘not at all willing to take risks’ and the value 10 means: ‘very willing to take risks.’ ” To assess the correlation of this risk question to choices over gambles, Dohmen et al. (2011, 532) recruit 450 subjects following the SOEP sampling procedure. Subjects are asked the SOEP risk question and, after completing

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a questionnaire similar to the standard SOEP questionnaire, participate in a paid lottery experiment. “[P]articipants were shown a table with 20 rows. In each row they had to decide whether they preferred a safe option or playing a lottery. In the lottery they could win either €300 or €0 with 50% probability (€1 ~US$ 1.2 at the time of the experiment). In each row the lottery was exactly the same, but the safe option increased from row to row. In the first row the safe option was 0, in the second it was 10, and so on up to 190 in row 20.” To ensure incentive compatibility, 1 of 7 participants had one of their rows randomly chosen for payment. A regression of the value of the safe option at the switching point on the general risk question shows a significant (and positive) relationship. More recently, Crosetto and Filippin (2013b) consider a between-subjects design where subjects do one of the following five incentivized risk measures: The Holt-Laury multiple-price list, the Eckel-Grossman task, the Gneezy-Potters investment game, the balloon analogue risk task (Lejuez et al. 2002) or the bomb risk elicitation task (Crosetto and Filippin 2013a).66 Every subject also answers the SOEP risk question described before and the DOSPERT (Blais and Weber 2006). They find that the SOEP question and the DOSPERT score are highly (and significantly) correlated (around 0.57). Comparing questionnaires with experimental outcomes, the SOEP correlates significantly with HL, EG, and the balloon task (though only with correlations of 0.23, 0.30 and 0.37, respectively.) For the investment game the correlation is 0.13 (not significant), and it is only 0.03 for the bomb task. Furthermore, “after running a linear regression of each choice on the observed demographics (age and gender) as a benchmark, we include each questionnaire separately in the regression, measuring the contribution of the last measure added to the adjusted R 2 ” (Crosetto and Filippin (2013b, 21). Only for the EG and the balloon task is the percentage point change in the adjusted R 2 positive (around 3 and 10, respectively). The results are similar when considering correlation with DOSPERT (though the balloon task is not significantly correlated with DORPERT).67 The fact that there are important domain-specific components in risk preferences is also evident in (nonexperimental) empirical work. For example, Einav and others (2012, 2636) consider individuals’ choices over five employer-provided insurance coverage decisions and one 401(k) investment decision. They consider ordinal rankings in the riskiness of choices of individuals and find that the average spearman rank correlation is 0.19. This is in large part due to the fact that the correlation between the 401(k) choice and any insurance decision is in general lower than 0.061. However, within insurance choices, there is a domain-general component to preferences that seems substantively important. “For example, we find that one’s choices in other insurance domains have about four times more predictive power for one’s choice in a given insurance domain than does a rich set of demographic variables” (Einav et al. 2012, 2636). A third issue when considering the robustness of a trait is whether within a domain and within an elicitation method there is stability over time. Specifically, will a subject show similar responses if asked to make the identical risk decision later? Andersen et al. (2008), using the Danish population, “find some variation in risk attitudes over time, but we do not detect a general tendency for risk attitudes to increase or decrease over a 17-month span.” There are not many studies that use a time frame of a year or more. One exception that, in addition, uses incentivized choices is Levin et al. (2007). Parents and their 6- to 8-year-old children complete a first set of risk experiments and then a follow-up roughly 3 years later. There are significant correlations in choices of both children and parents, though children’s choices become less correlated with those of their parents.

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V.E.2 CAN GENDER DIFFERENCES IN RISK ACCOUNT FOR GENDER DIFFERENCES IN ECONOMIC OUTCOMES? Despite all those hurdles, there have been some attempts to correlate risk measures estimated through experiments or questionnaires with choices outside the lab. The first paper I could find is by Ziller (1957). He correlates a risk measure using Swineford (1938; see Section V.A) with (expected) vocational choices of 182 sophomores from the University of Delaware Army ROTC program. Subjects who expect to work in sales showed the highest index for risk preference, followed by mechanical engineering and education, and those choosing engineering showed the least tolerance for risk. However, it is not clear per se how different jobs differ in their inherent amount of risk. An early economic paper relating risk measures to economic outcomes is Barsky et al. (1997), which finds that an nonincentivized risk question can predict various health risks (such as smoking and drinking), immigration status, self-employment, and whether the person holds stock. While they find gender differences in the risk question, they do not use them to ask whether gender differences in risk can help account for gender differences in economic outcomes. A notable line of work was started by Dohmen et al. (2011). They consider the hypothetical risk question asked on the 2004 SOEP: “How do you see yourself: are you generally a person who is fully prepared to take risks or do you try to avoid taking risks? Please tick the box on the scale, where the value 0 means: ‘not at all willing to take risks’ and the value 10 means: ‘very willing to take risks.’ ” A large fraction of the 22,019 individuals in 11,803 households of the 2004 SOEP answered the risk question as well as risk questions that asked about willingness to take risks in a specific context: car driving, financial matters, sports/leisure, career, and health. They find that women see themselves as less willing to take risk (by 0.6). Likewise, older people (in years) and shorter people (in centimeters) are also less willing to take risk, with coefficients about 5% of the gender coefficient.68 Most importantly “[a]ll of the survey measures are shown to explain various risky behaviors, including holding stocks, smoking, self-employment, and participation in active sports. The best all-round predictor is the general risk question. On the other hand, asking about risk attitudes in a more specific context gives a stronger measure for the corresponding context” (Dohmen et al. 2011, 542). Unfortunately, there is no direct analysis about the extent by which gender differences in behavior such as stock holding are accounted for by gender differences in the risk measure. Dohmen and Falk (2011, 585) exploit the fact that the 2004 SOEP also asked “whether the performance of a respondent is regularly evaluated in a formal procedure, a requisite element of performance contingent remuneration schemes.” They find that more-risktolerant workers, as measured by the SOEP question, are more likely to work in jobs with performance evaluation and that women are less likely to work for variable pay than men. Unfortunately, no direct link is given as to how much of the gender gap in work for variable pay could be accounted for by gender differences in risk tolerance. Dohmen et al. (2011) correlate the SOEP risk question with incentivized lottery choices of one set of participants, as well as with economic outcomes of participants in the 2004 SOEP. Of course, in and of itself, this does not imply that the reason the risk question predicts economic outcomes is due to the component that correlates with incentivized lottery choices. It could be that the risk question captures other behavioral attitudes of participants that, while correlated with behavior and economic outcomes, do not correlate with risk preferences.

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To assess whether the risk question correlates due to its capturing risk preferences, one could, for example, consider the behavior of subjects who both answer a risk question and provide data on an incentivized lottery choice. Lonnqvist et al. (2011) have participants play a trust game (see Section IV), make choices in an incentivized HL task, and answer the SOEP risk question, among others. The paper finds that the two measures of risk attitudes are uncorrelated, though both correlate with the decision of a trustor in a trust game. However, the coefficient of either risk measure on behavior of the trustor (the first mover in the trust game), and the impact of including a risk measure on the adjusted R 2 of the behavior of the trustor are virtually unaffected whether or not the other risk measure is already controlled for. This suggests that the two risk measures are almost orthogonal to each other in terms of accounting for behavior in the trust game, a fact that is already suggested by the lack of correlation between the two risk measures. Buser, Niederle, and Vesterlund (BNO; 2014), discussed in more detail in Section II, measured not only the competitiveness of almost 400 children in 4 schools in the Netherlands using a Niederle-Vesterlund elicitation method but also their risk attitudes. BNO used both an Eckel-Grossman task, where subjects could choose one of five gambles (a sure payoff of €2 and four 50–50 lotteries with increasing riskiness and expected payoffs: 3 or 1.5; 4 or 1; 5 or 0.5; 6 or 0) and the nonincentivized risk question used in the SOEP studied by Dohmen et al. (2011). BNO found that both risk measures are correlated with tournament entry choices. However, when assessing whether education choices are correlated with risk preferences, only the EG lottery measure was significantly correlated, while the nonincentivized risk question was not. Furthermore, including the EG risk question significantly reduced the gender gap in education choices, while the unincentivized risk question did not. That is, while risk preferences as measured by EG accounted for a significant fraction of the gender gap in education choices, this was not the case for the answer to the question, How do you see yourself: Are you generally a person who is fully prepared to take risks or do you try to avoid taking risks? Clearly this line of work needs to be expanded and needs to confirm that experimentally measured gender differences in risk preferences are able to account for gender differences in economic outcomes or choices. V.F An Example of a Careful Control for Risk Aversion Given that the first paper on gender differences in risk aversion discussed concerned decisions in a multiple-choice exam, the last paper discussed will close this loop and provide a modern view on the possible effect of gender differences in risk aversion in accounting for gender differences in exam grades. Multiple-choice exams are, in the United States, ubiquitous and important; a prime example is the SAT, which is required by many colleges. While SAT scores seem to predict college grades, women perform relatively worse on multiple-choice tests compared with essay questions, and their SAT scores underpredict their college performance (see references in Baldiga, 2013). Baldiga (2013) directly tests the extent to which gender differences in test taking (and scores) can be attributed to gender differences in risk aversion, as opposed to other effects, such as gender differences in ability or confidence. Subjects in her experiment first answered SATII US and World history practice questions, where each question had 4 (instead of 5, as the real SAT) possible answers. Subjects received 1 point for every correct answer. There are two treatments: In the no-penalty treatment, subjects were

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not penalized for wrong answers; in the penalty treatment, subjects were penalized by ¼ point for each wrong answer. In both treatments subjects earned 0 points for each skipped question. Therefore, in both treatments, a risk-neutral subject should answer all questions. In part II of the experiment, subjects were offered 20 gambles, aimed at assessing their attitudes toward lotteries that mimic the risk from answering questions on the part I test. Specifically, subjects answered gambles where they had a chance of winning 1 point (ranging from 25% to 100% chance of winning) and in the other event lost X points, where X = 0 for subjects in the no-penalty condition and X = 14 the penalty condition. Subjects could also decline the gamble and get 0 for sure. Accepting such a gamble with a 75% chance to win is akin to answering the SAT question when subjects are 75% confident that they know the correct answer. To assess knowledge, part III of the experiment had subjects answer the same questions from part I, but subjects were not allowed to skip questions. In addition, an incentivized measure of confidence was elicited using a belief-elicitation procedure that mimics a BDM as employed by Mobius et al. (2014). That is, for each question, participants provided the probability with which they thought their (forced) answer was correct.69 Subjects were paid for 1 of the 3 parts of the experiment. Beyond the difference in penalties for a wrong question, there were two additional treatment designs. One was the no-frame treatment, while the frame treatment emphasized that the questions were SATII practice questions. This could make a difference since participants were US college students who presumably received a lot of coaching on how to approach SATs, and, as such, may have internalized not to skip questions. Baldiga shows that in the no-penalty condition, basically no one skips questions. In the penalty condition without a frame, men skip 2 questions (1 with SAT frame), compared to the 3.7 (2 with SAT frame) questions skipped by women, a significant difference in both cases. Women are about 6.5 percentage points more likely to skip a question, where about 10% of this gap can be accounted for by gender differences in knowledge as measured by part III. Therefore, women are still about 6 percentage points more likely to skip a question compared to men.70 While beliefs are found to predict whether a subject answered correctly, there are no gender differences in beliefs conditional on measured knowledge of the material. Conditional on beliefs of knowing the answer in part III, women are more likely to skip that same question in part I then men are. In fact, the gender gap on question skipping is hardly affected by controlling for beliefs and remains significant at 5.9 percentage points. Concerning risk, women are significantly more risk averse then men in the penalty treatment. The mean probability of success of the riskiest bet taken by men is a 39.46% chance of winning, compared to 43.44% for women.71 Regressions confirm that risk accounts for roughly one-third of the gender gap in skipping questions; however, the remaining gap of 4 percentage points is still significant. So, while gender differences in risk account for a significant portion, about one-third of the gender gap in SAT test taking, the results suggest that it may be far too hasty to attribute the whole gender gap to risk aversion. Baldiga (2013) then studies the impact of the gender difference of question skipping on the final score and shows that as a result, women receive lower test scores than men with the same knowledge of material. Specifically, women score about 0.4 point worse 1 of a standard deviation in on the 20-point test, which corresponds to approximately 12 part I scores. This result is perhaps a great example how a small gender difference in question skipping—6 percentage points, of which about 2 can be attributed to gender

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differences in risk aversion—can accumulate over a longer test to much larger total effect. Recently, Tannenbaum (2012) analyzed data from a subsample of the fall 2001 mathematics SAT and found that women skip significantly more questions than men. The paper exploits variations in the penalties for answering a question wrongly and confirms the conclusion of Baldiga that roughly 40% of the gender gap in test scores can be attributed to gender differences in risk aversion. The risk assessment used by Baldiga can serve as guidance on how to handle the question of whether gender differences in risk aversion can account for gender differences in the question or task at hand. Specifically, the risk assessment very nicely complemented the belief question on chances of answering a question correctly. It would, of course, not be justified to consider the exact portion of the gender gap in question skipping attributable to gender differences in risk aversion as a fixed constant for all environments and subjects. However, the paper provides a strong piece of evidence that in an environment in which gender differences in performance in risky environments are important, gender differences in risk aversion may be far from accounting for the total difference, or perhaps even the majority, of the gender gap. Such an approach to directly measure the impact of risk aversion on gender differences in specific tasks has been also employed by Gneezy, Niederle, and Rustichini (GNR; 2003) and Niederle and Vesterlund (NV; 2007) discussed in Section II. In both papers, the test for risk aversion consisted of a treatment by elimination: A control treatment was constructed that mirrored the decision of interest and retained risk but eliminated competition. The result was that compared to a treatment where competitive motives played a role, the gender gap was either significantly reduced or not significant. Such a direct approach using experimental design rather than specific methods that elicit risk preferences in general may be more desirable whenever it is not obvious what the right risk elicitation method is. This is especially an issue because different riskelicitation methods reliably generate gender gaps of different magnitude, from large to nonexistent, and hence using different elicitation methods could produce different results when added in regressions that estimate the gender gap in the variable of interest. V.G Conclusions Throughout this chapter, I have provided examples of papers where the control for risk aversion was germane to the task at hand, which, however, does not allow to compute specific parameters of risk aversion; see, for example, Gneezy, Niederle, and Rustichini (2003) and Niederle and Vesterlund (2007) in Section II. Overall, gender differences in preferences toward risky prospects seem to exist, though they vary considerably depending on the elicitation method. Some methods such as the Eckel-Grossman task (Eckel and Grossman 2002) quite reliably produce results where women behave as if they are more risk averse. Others, such as the Holt-Laury method (Holt and Laury 2002), in general do not find that women are significantly more risk averse than men. A metastudy by Filippin and Crosetto (2014), including several thousands of women and men, found a statistically significant gender difference, with women being more risk averse. However, the gender gap is only about 16% of a standard deviation, and assuming a normal distributions of risk preferences, if a random man and a random woman are compared, there would be a 53% chance of being correct when saying that the more risk averse of the two is a woman. Therefore, experiments with several hundred subjects may not reliably find gender differences in risk aversion.

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More work is needed to understand the exact nature of gender differences in risk aversion. This heterogeneity of results on gender differences in risk aversion is also present when considering whether a risk parameter has external relevance, and which elicitation method is most likely to capture a risk parameter that can account for various economic outcomes. Finally, the heterogeneity of results on gender differences in risk aversion suggests that an experiment should probably employ an elicitation method that is germane to the task in question. At the very least, it suggests that gender differences in various experiments cannot automatically be attributed to gender differences in risk aversion.

VI CONCLUSIONS The last decade has seen an explosion of experiments documenting gender differences in behavior. In this chapter I focused on only three such traits: attitudes to competition, altruism or cooperation, and risk. While gender differences are large and robust in attitudes to competition, they are at times small for cooperative and altruistic attitudes. This seems to be at odds with the “common wisdom” and with some of the perhaps too-strongly formulated conclusions of previous summaries of the literature. One insight into the causes for the discrepancy between documented results and beliefs can be gained from Eckel and Grossman (2002, 286). They had subjects choose 1 out of 5 gambles, where choice 1 was a certain payoff of $16, while choices 2–5 were 50–50 gambles of dollar amounts (24, 12), (32, 8), (40, 4) and (48, 0), respectively. They had subjects not only pick a choice for themselves, but also guess what choices others made. “For the forecasting task, each subject stood in turn and was visible to all others in the room. The other subjects indicated on their prediction forms which of the five choices they thought the standing person had chosen. For every correct prediction, they received a $1 bonus. Forms were collected and matched with decisions, and payoffs for this task were calculated.” “[T]here was consensus between the sexes regarding men’s risk aversion but not women’s. The mean predictions for men did not differ significantly by sex (3.33 by men vs. 3.26 by women, t = 1.06, p = ns), but men under-predicted women’s risk acceptance even more than did women (2.48 and 2.61, respectively, t = 2.12, p < .02)” (p. 289). The results suggest that men believe the gender gap in risk aversion to be larger than females do, who, in turn, do not overestimate the gender gap. The literature on belief differences between different groups of subjects is still in its early stages, though for notable early work, see Fershtman and Gneezy (2001), Mobius and Rosenblatt (2006), and Bohnet, van Geen, and Bazerman (forthcoming). It may very well be that for many traits, both women and men have beliefs that exacerbate the existing gender gap.72 While clear results on gender differences in preferences start to emerge, there is still work to do concerning the external validity of findings. For example, which measures of risk aversion are correlated with choices in other tasks, and which are better able to predict behavior out of sample? The biggest gap in the literature, however, concerns the external relevance of laboratory findings. To date there have been few data sets and papers combining traits with behavior outside the laboratory and even fewer assessing whether gender differences in a trait that can account for gender differences in economic outcomes. One way to facilitate such endeavors is to provide more research linking easy-touse hypothetical measures with incentivized experimental measures. That is, to what

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extent is a nonincentivized hypothetical choice such as, Do you think of yourself as someone who is eager to participate in competitions? or a nonchoice measure such as, Do you enjoy being in a competition correlated with incentivized tournamententry decisions à la Niederle and Vesterlund (2007)? And, more importantly, when predicting behavior out of sample or in a different environment, how much is lost when using hypothetical or nonchoice measures compared to incentivized measures? Note that for such nonincentivized measures to be useful, three criteria have to be fulfilled. First, nonincentivized measures as well as incentivized measures have to correlate with choices outside of the laboratory. Second nonincentivized measures have to correlate with incentivized measures. Third, and perhaps most importantly, there has to be evidence that the nonincentivized measure captures some variation of behavior associated with the incentivized measure and, ideally, not much more. Specifically, it should certainly not be the case that when including both the incentivized and the nonincentivized measure, they act as if they were two orthogonal measures of economic behavior. Evidence linking behavioral traits with behavior outside of the laboratory is crucial to demonstrate the value of behavioral corresponding laboratory experiments. I hope that the next Handbook of Experimental Economics will have sufficient work that there could be a chapter covering the external relevance of behavioral traits.

ACKNOWLEDGMENTS I am deeply grateful to Katherine Coffman and John Kagel for their extensive comments and to John Kagel and Alvin Roth for their patience. Foremost, I am thankful to Lise Vesterlund, with whom I have most frequently worked on gender. Our long discussions have shaped my understanding of the topic tremendously. The first section of this chapter is based on our common work, and I have borrowed from it extensively. Finally, I am grateful to the NSF for its support.

NOTES 1. For example, Simons and Levin (1998, 648), when studying change blindness, the failure to detect changes when interacting with an individual, such as exchanging the clothes of that person or exchanging the person herself or himself, confine themselves to exchanging a person with a person of the same sex. They write that, “Clearly we would be quite surprised if subjects missed a switch between enormously different people (e.g., a switch from a 4-ft 9-in. female of one race to a 6-ft 5-in. male of another). The change in this case would alter not only the visual details of the person, but also her or his category membership. If, as suggested by other recent findings of change blindness, we retain only abstracted information and not visual details from one view to the next, changes to category membership may well be detectable.” 2. The 50 million estimated sales were reported on Wikipedia, and the CNN article that ranks the most popular books in the 1990s is here: http://archives.cnn.com/1999/books/news/12/31/1990.sellers/index.html. 3. For the importance of replication in all fields, not only experimental economics, see, for example, Coffman and Niederle (2015). Coffman and Niederle (2016) discuss ways to promote replications and studies of robustness in experimental economics. 4. For example, there has been a long and ongoing debate on gender differences in charitable donations with, at present, no clear conclusion. An even more indirect test from the field consists of explaining voting patterns of women and men. For example, Edlund and Pande (2002) show that over time, women have become more left wing. Their paper points out that this difference may, however, be explained by an increase in divorce risk and decline in marriage. That is a preference for redistributive policies could have purely economic rather than psychological reasons. More recently though, Funk and Gathmann (2015)

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5. 6.

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provide some evidence that gender differences in voting remain after controlling for socioeconomic characteristics. For a review on the literature on debiasing, see Soll, Milkman, and Payne (forthcoming). I am very indebted to Lise Vesterlund for numerous discussions on this topic and for her work on our previous survey paper, Niederle and Vesterlund (2011), from which I drew heavily to write the present one. Keeping subjects completely in the dark about the gender of their opponent may lead to subjects each forming different beliefs about the gender of their opponent, which in itself could lead to differences in the behavior of a participant. By paying the tournament winner depending on the performance rather than a fixed prize, NV avoid providing information about winning performances or distorting incentives for very high performing individuals. This is supported by the fact that subjects who in treatment 3 choose the piece-rate scheme have the same change in performance between treatment 2 and treatment 3 than those who chose the tournament in treatment 3. Note that the results do not imply that participants do not provide a high effort in the tournament; rather it appears that either their baseline effort is already quite high or that the task is one in which changes in effort do not result in large changes in performance. If we add the subjects whose payoff would be basically identical under a piece rate and a tournament incentive scheme (because their chance of winning the tournament is roughly 25%), then 40% of women and 45% of men have higher or basically identical earnings from a tournament payment. Similar results are obtained when NV consider the performance after the entry decision. Specifically, Healy and Pate (2011) and Niederle, Segal, and Vesterlund (2013) find that when subjects decide whether to submit their treatment 1 piece-rate performance to a competitive payment scheme, there is no gender difference in choices when controlling for absolute as well as beliefs about relative treatment 1 piece-rate performance. Dargnies (2012), Healy and Pate (2011), and Niederle, Segal, and Vesterlund (2013) show that gender differences in tournament entry in treatment 3 are not very affected when controlling for the treatment 4 choice in addition to absolute as well as beliefs about relative treatment 2 tournament performance. Eriksson, Teyssier and Villeval (2009) have participants select an incentive scheme using a standard experimental design in which agents do not perform in a task but instead pick effort using given cost functions and corresponding performance distributions. They find no gender differences in tournament entry when controlling for risk, which is negatively correlated with tournament entry. Balafoutas, Kerschbamer, and Sutter (2012) show that risk attitudes correlate with tournament entry, but it is not clear how much it affects the gender gap in tournament entry. Dreber, von Essen, and Ranehill (2014) found that adding beliefs renders the gender gap in tournament entry in a math task insignificant. Controlling for risk further reduces the gender gap. While males often score better on abstract math problems, there is no gender difference in arithmetic or algebra performance. Women tend to score better than men on computational problems (see Hyde, Fennema, and Lamon (1990) for a meta-analysis of 100 studies on gender differences in math performance). In psychology, priming studies have recently come under scrutiny and are often hard to replicate (e.g., Klein et al. 2014). Since 2 out of 6 competitors win the tournament at a payment of 3 times the piece rate, a risk-neutral participant who believes that all competitors are equally likely to win the tournament is, for a given performance, indifferent between the piece rate and the tournament pay, just like in NV. The task of adding up 5 two-digit numbers for 5 minutes does not fit that bill. Rather, this seems to be a task where changes in the incentive scheme don’t lead to large changes in performance, though there may still be (hard to observe) changes in effort. Other reasons include that women are not sensitive to the incentive scheme at all and always perform similarly. It could also be that women see not increasing the performance in the tournament compared to the random-pay treatment like contributing to a public good. If all participants have a 16 chance of winning, then they would be better off if all wouldn’t increase performance. An alternative hypothesis is that women believe that there is a stereotype that they should not be able to perform well in this task or in competition against men, and hence they may suffer from stereotype threat (Steele 1997), which provides an additional source of anxiety while performing the task and yields higher instances of “choking under pressure.” A single-sex piece-rate treatment confirms that women perform highly when competing against women and not merely when there are no men in the group of participants (though note that the experimenter was always male, Uri Gneezy).

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22. In terms of the positive effects of affirmative action on performance, Calsamiglia, Franke, and Rey Biel (2013) find positive effects of affirmative action in the performance (effort) in tournaments that have children with prior experience in the task at hand compete against children with no prior experience. See also Schotter and Weigelt (1992) for experiments in an abstract setting. 23. “Teammates must jointly agree on a choice having (almost) continuous access to a messaging program that allows for bilateral communication about possible actions. Both teammates receive the full payout from their team’s outcomes” (Cooper and Kagel 2013, 9). 24. Cooper and Kagel (2013, 6) note that “An odd feature of our data supports this connection: while women who have played strategically are significantly less likely to provide strategic advice than men, women who have not played strategically are significantly more likely to provide strategic advice than men who have not played strategically. It seems that men who have figured out to play strategically follow through both by playing strategically and by giving advice to play strategically. Women are more cautious, often only doing one or the other.” 25. Eagly and Crowley (1986) further argue based on social-role theory that some kinds of helping are part of the male role, such as when helping is heroic or chivalrous, and such behavior is likely to be facilitated when there are onlookers around. However, women’s helping is more nurturing and caring, such as caring for children, and often occurs in private. Dividing studies into those where onlookers were present and when they were not, they found men helped much more than women did with onlookers around (d = 0.74) while there were essentially no gender differences without onlookers (d = −0.02). 26. Specifically, they consider dictator games where, instead of a range of giving that is only positive, subjects can also take money away. They find that more subjects take money away compared to the number of subjects who gave 0 in a standard dictator game. See Cooper and Kagel (Chapter 4) for further discussion of the stability of dictator game outcomes. 27. They consider two public good games with interior dominant strategies and efficient outcomes, where in one game the interior equilibrium is above 5 and below 5 in the other. They show that especially among participants who decide more quickly than others on how much to contribute to the public good, a large fraction centers around 5. These “fast” participants are “more generous” than “slow deciders” if the dominant strategy equilibrium is less than 5 and “less generous” if the dominant strategy equilibrium is higher than 5. The paper shows that speed of decision is not necessarily correlated with generosity. This view has gained momentum, with Kahneman (2011) arguing that intuitive choices should be faster, which has been interpreted as fast choices being more intuitive (and altruistic); see Rand, Greene, and Nowak (2012). For a recent comprehensive study that shows that over time participants become more generous when giving is cheap and less generous when giving is expensive, see Kessler, Kivimaki and Niederle (2016). 28. The early literature on public goods has shown that some, but not all, giving in repeated public good games can be attributed to confusion (Andreoni 1995). 29. In a typical ultimatum game, a proposer offers to divide a fixed amount of money between herself or himself and the responder. The responder can accept the ultimatum proposal, in which case the division is implemented, or reject it, in which case both players receive nothing. In a typical trust game, the proposer can pass any number of tokens x from her or his endowment m to a responder, where tokens passed to the responder are often tripled. The responder can then give some tokens y back to the proposer, from zero to all the 3x tokens, where tokens returned are not multiplied anymore. This leaves the proposer (or trustor) with m − x + y tokens and the responder (trustee) with 3x − y. General outcomes in these games are also reviewed in Cooper and Kagel (Chapter 4). 30. There also has been a lively debate about whether behavior in the trust game, especially for the first movers, reflects their “altruistic” or “trusting” tendencies versus, for example, their attitudes toward risk; see Bohnet, Herrmann, and Zeckhauser (2010, 826), who write, “ . . . differences in willingness to trust mainly came from differences in people’s intolerance of betrayal, though for men differences in willingness to take risk also contributed.” Other work finds that the behavior of the second mover in the trust game is better predicted by survey questions on trust rather than trustworthiness; for example, Glaeser et al. (2000, 840) write, “In summary, to determine whether someone is trusting, ask him about specific instances of past trusting behaviors. To determine whether someone is trustworthy, ask him if he trusts others.” 31. About 50 subjects played dictator games where they could offer any dollar amount from 0 to 5 to the other player, of which half played only one dictator game; the others played 10 dictator games over $1 simultaneously. The remaining 25 subjects could offer only half or nothing and also played 10 $1 dictator games simultaneously. They found no gender difference in each treatment separately. 32. He also includes “4 papers to come out in 2010 but already available through advance access. 4 papers do not report sample size. The remaining papers cover a total of 41,433 observations.”

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Chapter 8 33. They write in their abstract that “women are more sensitive than men to the costs of generous actions when deciding whether to be generous.” While this reads as if they do not replicate Andreoni and Vesterlund (2001), a more careful reading of their paper reveals that Cox and Deck do not consider variation in the price of giving, but rather variation in total payoff—or the pie to be distributed (holding the price of giving constant at a 1:1 rate). They find that women respond more to a reduction in their budget than men do. 34. The presented results are over 7 different payoff matrices. 35. See previous material for a discussion of Cohen’s d-value for effect size. 36. “Several articles reported a null relationship between sex and cooperation but failed to provide the statistics necessary to calculate the effect size. We estimated that these studies had an effect size of zero. This is a very conservative estimate, as several of these articles observed a mean difference between men and women but lacked the statistical power to detect a small effect size. Therefore, for all analyses, we first report the results, excluding the null findings coded as zero effect size, followed by an additional analysis including these estimated null findings” (Balliet et al. 2011, 887). In the stem-and-leaf plot these studies are omitted. 37. They note, however, that the conclusions differ when using a fixed-effects rather than random-effects analysis, in which case women are significantly more cooperative than men, but with an “exceptionally small effect size (d = −0.04). 38. For an early paper on gender differences in strategic environments, see Casari, Ham, and Kagel (2007). They study bidding in common value auctions and find that women suffer from a stronger winner’s curse than men to begin with but eventually catch up as they learn faster. 39. “This explains why Holt (1986) and Karni and Safra (1987) found the RPS mechanism not to be incentive compatible: they both assume reduction of compound lotteries and non-expected utility preferences” (Azrieli, Chambers, and Healy 2014, 13). 40. Azrieli, Chambers, and Healy (2014, 16) compare papers that study paying for one decision randomly in a long multiple- price list to paying for only one decision. They write, “In all of these direct-comparison studies, subjects who are given a single choice do not see the other decision problems. Thus, behavior differences may be attributed to framing effects (causing a change in underlying preferences) rather than monotonicity violations. Disentangling these confounded explanations is clearly important. In our view, Cubitt, Starmer, and Sugden (1998, Experiment 3) provides the cleanest test of incentive compatibility of the RPS mechanism because the confound with framing is eliminated. Subjects are randomly assigned to one of three groups. All groups are given the same 20 decision problems. The first group is paid only for D1; the second group only for D2; and the third group is paid for one randomly selected problem out of the twenty, each selected with equal probability. Choice frequencies in D1 do not significantly differ between groups one and three (Chi-square p-value of 0.355) and choice frequencies in D2 do not differ between groups two and three (Chi-square p-value of 0.285). Thus incentive compatibility of the RPS mechanism holds for that experiment.” 41. The reason to use only those questions for which the pupil asked for 4 points is that Swineford (1938, 299) showed that the number of 4s asked for were less likely to be 0s than for any other number of points and that “[T]the correlation between the number of ‘4’s’ on the odd and even items is .911 and that for the ‘3’s’ is .788.” 42. An additional 74 boys and 39 girls were eliminated from the study “either because on one or more of these tests no extra credits were requested, or because on one or more tests no errors were made among the items attempted” (p. 439). For these children, Swineford’s gambling measure is either not defined, or zero. It is not clear how those are distributed between girls and boys. 43. “The S’s were 52 preschool and elementary school children evenly divided by sex” (p. 578). 44. “You see how each machine works? Now I am going to give you 14 pennies. You can use these pennies and the pennies you get out of the machine to play with. At the end of the game you can use the pennies you have won to buy prizes. Now you can play the game. You can play any machine you want or you can play all the machines. I’ll tell you when to stop. Remember, the more pennies you have at the end of the game, the better the prize you can buy with your pennies” (pp. 579, 580). 45. Note, though, that all machines had an expected return of 0. Perhaps a summary of this paper (given after the first result concerning the free choice in the last 30 trials) is, “The significant findings of this study are related to sex differences in probability preference. In a free choice, repetitive play situation, boys preferred probabilities of winning involving greater risk than did girls” (pp. 580–81). 46. Slovic (1966, 170) cites two other papers that provide evidence that boys are willing to take greater risks than girls. Of those, one observes children in the playground or home and the other finds that “boys were less ready to withdraw from threat of failure on an intellectual-achievement task than girls were.”

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47. The authors use several steps to aim to retrieve all papers on gender differences in risk aversion published between 1967 and 1997, using PsycINFO and PsycLIT by searching for risk or risk taking and gender differences or sex differences and then searching in MEDLINE using terms associated with specific risks, such as smoking, driving, and framing effects, and finally searching Dissertation Abstracts. 48. When considering individual effect sizes, note that the first quintile of effect sizes is −1.23 to −0.09, and the second is −0.08 to 0.07 “indicating essentially no difference.” The authors conclude, hence, that “a sizable minority (i.e.. 40%) were either negative [that is, men are more risk averse] or close to zero” (Byrnes, Miller, and Schafer 1999, 372). The intervals for the third, fourth, and fifth quintiles were 0.08 to 0.27, 0.28 to 0.49, and 0.50 to 1.45, respectively. 49. Put differently, to find that women are more risk averse than men with a p-value of 0.1 using a two-sided t-test and a power level of 0.8, one would need roughly 700 women and 700 men in one’s sample. 50. The oldest two studies in the survey, and also the oldest using “gambling tasks,” were published in 1964, a book by Kogan and Wallach and the paper by Kass (1964) described earlier. 51. The others use tasks such as: informed guessing, where “participants could earn points or money for correct guesses but could also lose points or money for incorrect guesses (e.g., standardized achievement tests that have penalties for incorrect guesses); physical activity included behavior such as “climbing a steep embankment, playing in the street, trying out gymnastics equipment . . . and taking a ride on an animal (e.g., a donkey)”; driving includes “taking a left turn in front of incoming traffic, gliding through a stop sign rather than coming to a complete stop and engaging in simulated driving tasks”; physical skills described “playing shuffleboard or tossing rings onto pegs. In most cases, options differed in terms of their probability of success . . . and the number of points that could be won or lost”; risky experiments “involved an individual’s willingness to participate in an experiment that was described to them as involving the chance of physical or psychological harm”; intellectual risk taking “involved tasks that required mathematical or spatial reasoning skills. Participants were presented with items of various levels of difficulty and asked to indicate their preferred level of choice. Unlike the tasks in the informed guessing category, points were not subtracted for incorrect answers on the intellectual tasks. Thus participants were mainly concerned about getting stuck on items or exposing their lack of skill when they fail.” The final category is all the rest and includes “lying about finding someone else’s money, cheating during a computerized game, . . . and administering an electric shock to a confederate to increase his learning rate.” The category gambling task is the category closest to experimental economics tasks, and is described as “similar to the category of physical skills in terms of the varied risks/reward options.” However, “a person’s skill level had no bearing on the likelihood of success” (Byrnes, Miller, and Schafer. 1999, 371). 52. The Kass (1964) study is coded as (d = 0.80, n Mal e = 21, n F emal e = 21). (While Kass (1964) mentions 52 participants in the paper, the abstract describes the study as including 21 boys and 21 girls.) While d = 0.80 represents the choices in the last 30 trials, this is the only analysis where the data were described, so the fact that the (presumable) lack of a gender gap in the forced choice part of the experiment is not represented is no fault of Byrnes, Miller, and Schafer (1999). 53. Eckel and Grossman (2002, 286) had both a gain and a loss treatment. In the “loss aversion” treatment, subjects first received $6, and all payoffs from the table were reduced by 6. “Subjects in the Loss treatment were informed that if they selected . . . either Gamble 4 or 5 and Event B occurs, your losses will be deducted from your $6 fee for completing the survey” One hundred forty-nine students participated in the loss treatment (eight sessions) and 55 participated in the no-loss treatment (five sessions). They found no difference between the loss and the gain frame for either men or women and hence pool the data across treatments. 54. Interestingly, Eckel and Grossman (2008c) do not cite the survey by Byrnes et al. (1999). Only one of the studies included in this reference was summarized by Eckel and Grossman (2008c), who, in turn, include two studies published in 1995 and 1997 (one in William and Mary Journal of Women and the Law and the other in the Journal of Economic Psychology) that were not included in Byrnes, Miller, and Schafer. Furthermore, Eckel and Grossman have two papers, Eckel and Grossman (2002) and Eckel and Grossman (2008a), that are always mentioned together. It seems that the data from Eckel and Grossman (2008a) are (almost) the same as those of Eckel and Grossman (2002); the former has 261 subjects and the latter has 204, though no paper cites the other. 55. Croson and Gneezy (2009, 449) write that the study “finds no significant risk differences in estimations of prospect-theory preferences (no gender differences in loss aversion or in the curvature of the value function). However, they do not report gender differences in risk aversion parameters from traditional expected utility models.” 56. Note that of the 6 papers cited by Eckel and Grossman (2008c) that found no gender difference in risk aversion, 3 were at the time already published in economics journals.

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Chapter 8 57. Interestingly, in the Croson and Gneezy (2009) survey, it was not used as an example of gender differences in risk aversion. 58. Nelson (2013) criticizes Charness and Gneezy (2012) by pointing out that average differences may not necessarily translate into significant differences, and those in turn may not necessarily translate to large economic differences on the individual level. She computes Cohen’s d for studies found in Charness and Gneezy; the results are given shortly. The paper also provides tests pertaining to the significance of gender differences and shows that in many papers in Charness and Gneezy, while women invest less than men, those differences are not significant. 59. A query on January 1, 2013 on Scopus bibliographic database revealed that Holt and Laury (2002) had been cited 528 times, and they found another 26 working papers through conferences and the Economics Science Association discussion group. “We regard as comparable the multiple choice lists in which the amount at stake is held constant while the increase in the expected value of the lotteries is obtained through a higher probability of the good outcome.” While 48 papers were not accessible to them, 118 publications (and 17 working papers) replicate Holt and Laury’s method, of which 94 publication have their own data set and have data for both male and female subjects. Of the 94 papers and 17 working papers, they were able to obtain the data from 54 publications and 9 working papers, of which 48 and 6, respectively, shared microdata and not just summary statistics. When a subject in an experiment made multiple Holt and Laury choices, then, for each subject, only the first such test was chosen. 60. So, in the usual HL task, as in Table 8.3 of Section V.B, a subject makes 6 safe choices if in the sixth row 7 she chooses option A but chooses option B when the chance of the high outcome is 10 . 61. “Females are significantly more likely to be inconsistent” (Filippin and Crosetto 2014, 17). About 14% of subjects switch from option B to option A, where this is done by 12.1% of males but 15.8% of females. “Inconsistent subjects make on average 5.15 safe choices, without significant gender differences (Mann Whitney test, p = 0.67). This number is lower than that of consistent subjects (5.63), and significantly so (Mann Whitney test, p < 0.001). At first glance this seems to suggest that inconsistent subjects tend to systematically bias downward the number of safe choices. However a more careful interpretation suggests that inconsistent subjects simply tend to make choices that are closer to a random decision, which in the framework of the HL [Holt and Laury] task coincides with choosing each option half of the times” (p. 18). 62. “For the investment game we use Cohen’s d computed by Nelson (2013) for all studies included in the survey paper by Charness and Gneezy (2012). For the Eckel and Grossman task we use the data provided by the papers replicating the task, when available. In both cases we add the Cohen’s d computed from our own data presented in Crosetto and Filippin (2013b, 19).” 63. For early economic papers check out, for example, Harrison (1990), who used different elicitation methods across similar subjects and found different elicited risk measures, and Isaac and James (2000), who estimated individual risk preferences based on two games (and many assumptions) and found that different methods yielded not only different risk estimates, but also different rankings of which subjects are the most risk averse. 64. For two earlier, but more limited in scope, investigations, see Kogan and Wallach (1960) and Wallach and Kogan (1961). 65. For evidence using a between-subject design, see Harrison, List, and Towe (2007). 66. The balloon risk analog task technically has balls drawn from an urn, where n − 1 balls are safe and one is not. The task is visualized in that participants pump air into a ball and receive money each time they do so. Subjects can decide to stop pumping and collect their earnings. If they continue and the ball explodes (that is, when the unsafe ball is drawn from the urn), subjects earn 0. Subjects are, in general, not informed what n is (i.e., how many safe balls there are in the urn. The bomb risk elicitation task is similar, only now subjects are confronted with 100 boxes, know that one of them contains “the bomb,” and basically decide how many boxes to open. That is, it allows for a “strategy-method” implementation (since the bomb is detected only after subjects decided how many boxes to open), though subjects, through waiting, draw more boxes to open. Second, subjects are informed at any moment how many boxes they already have chosen to be opened later. 67. For other papers that find weak correlations of risk preferences across tasks, see, for example, Bruner (2009), Reynaud and Couture (2012), and Andreoni and Sprenger (2011). 68. These results are robust when including control variables for income and wealth. 69. After eliciting the chance Z with which the answer was correct, a random number R was drawn. If R < Z or R = Z, then the “final” answer was the subject’s answer. If R > Z, then the final answer was the correct answer with probability R. Subjects received 1 point if the final answer was correct. If the final answer was wrong, they lost X points, where X = 0 in the no- penalty condition and X = 14 in the penalty condition.

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70. The low impact of knowledge isn’t surprising, since on average, when subjects aren’t allowed to skip questions, women have 11.9 correct answers compared to 12.7 for men. 71. Note that the gender differences in question skipping seem not to be driven by gender differences in ambiguity aversion. Clearly, deciding to answer a question is a more ambiguous gamble than the gambles faced by subjects in part II of the experiment. Ambiguity aversion would suggest that subjects would be more likely to decline the ambiguous gamble (i.e., not answer a question) than the objective gamble in part II. However, Baldiga (2013) finds that subjects are in general more willing to accept the ambiguous gambles. 72. Bordalo et al. (forthcoming) suggest a simple mechanism for how stereotyping can exacerbate existing differences.

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9 Auctions A SURVEY OF EXPERIMENTAL RESEARCH

John H. Kagel and Dan Levin

INTRODUCTION The first question faced in writing this survey is how to organize it and what to include. There have been hundreds of papers reporting experimental work on auctions since the 1995 survey published in the first Handbook of Experimental Economics (Kagel 1995) so that it is quite impossible, and not very useful, to cover them all. Early theoretical and experimental research on auctions was restricted to simple environments with a fixed and commonly known number of bidders, each demanding a single unit. Accordingly, the 1995 survey focused on the revenue equivalence theorem with respect to independent-private-value (IPV) auctions, with research on common value auctions largely restricted to demonstrating the overwhelming presence of a winner’s curse. The present survey takes up where the other one left off. Section I reviews work since then on single-unit IPV auctions. Much of this research continues to be concerned with bidding above the risk-neutral Nash equilibrium (RNNE) in first-price sealed-bid (FPSB) auctions, work that is covered in Sections 1.1 and 1.2. Empirical economists have developed techniques for analyzing field data on auctions that are designed to uncover the underlying distribution of bidder values. Section 1.3 looks at an econometric analysis designed to investigate the validity of these techniques using experimental data where, unlike in field data, the underlying distribution of bidder values is known and can be compared to the implied probability distribution. Recent work on second-price sealedbid (SPSB) auctions is reported in Section 1.4. Section 1.5 reviews work on auctions with asymmetric valuation structures, where weak and strong bidders compete against each other. Section 1.6 reviews work on procurement auctions (where the low bid wins), dealing with some of the practices that are peculiar to that environment. Experiments investigating the role of cash balances and outside earnings on bids are reported in Section 1.7. Section 1.8 visits an important methodological issue related to analyzing experimental outcomes in auctions and other repeated trial settings. Section II reviews work on single-unit common value (CV) auctions. Sections 2.1–2.3 review studies investigating some of the important comparative static predictions of

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the theory; the ability of English auctions to raise revenue compared to FPSB auctions, the effect of a bidder with superior information (an insider) on auction revenue, and bidding in almost common-value auctions (where one bidder has a small private-value advantage for the item). Section 2.4 looks at results from the closely related “takeover” game, with a focus on sorting out between recent theories designed to explain the winner’s curse. Section 2.5 ties up some loose ends: Examining the behavior of super experienced bidders (e.g., is the persistent bidding above the RNNE a best response to rivals who are bidding more aggressively?), bidding in auctions with both common and private-value elements for all bidders, the role of selection bias, demographic and ability effects on the presence of a winner’s curse (e.g., do “smarter” subjects bid closer to the Nash prediction and/or make more money?), and the extent to which the winner’s curse extends beyond the lab to field settings. Section III takes up multiunit-demand auctions—auctions in which bidders demand more than a single unit of the items being sold. Much of the work here has been spurred by the Federal Communications Commission’s sale of spectrum (airwave) rights, beginning in the early 1990s, and the explosion of theoretical and applied research that followed. Section 3.1 looks at bidding in uniform price and Vickrey auctions for substitute goods. The experiments here are concerned with the issue of demand reduction in the uniform price auctions, and the ability of the Vickrey mechanism to correct for this. Section 3.2 extends the study of multiunit-demand Vickrey auctions to different ways of implementing the Vickrey auction—dynamic versus static mechanisms. Multiunit-demand auctions with synergies are covered in Section 3.3, with sequential multiunit-demand auctions covered in Section 3.4. Mechanism design studies that deal primarily with the thorny issues associated with package bidding are covered in Chapter 5. Section IV deals with issues that do not fit in neatly elsewhere: collusion, an everpresent concern in auctions (Section 4.1), selling multiple units simultaneously to bidders who demand only a single unit (Section 4.2), Internet auctions (Section 4.3), and entry into auctions (Section 4.4). The literature is much more extensive and less focused this time around than in the 1995 survey. The good news is that it covers a lot of new ground. The bad news is that we cannot hope to cover all of the good papers out there. Our hope is that we have surveyed enough of the more important developments in enough detail for both the novice and experienced reader to benefit from the survey and that we provide a summary of established knowledge where it exists, while not leaving out too much of importance.

I SINGLE-UNIT PRIVATE VALUE AUCTIONS Initial experimental research on auctions focused on the independent private values (IPV) model, with particular focus on the revenue equivalence theorem (RET). In the IPV model each bidder privately observes his or her own valuation (known with certainty), bidders’ valuations are drawn independently from the same commonly known distribution function, and the number of bidders is known. Under the RET (Myerson 1981; Riley and Samuelson 1981) the four main auction formats—first- and second-price sealed-bid auctions, English and Dutch auctions—yield the same average revenue, assuming the same number of risk-neutral bidders and the same reserve price.1 Further, FPSB and Dutch auctions, as well as SPSB and English auctions, are

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theoretically isomorphic to each other, yielding not just the same ex ante expected revenue but also the same revenue in any realization of bidders’ signals. These two isomorphisms are particularly attractive as they do not depend on risk neutrality (as does the more general RET), which makes for more robust investigations of the theory’s predictions. An experimental session typically consists of several auction periods under a given auction institution. Subjects’ valuations are determined randomly prior to each auction with valuations being independent draws (iid) from the same distribution, typically a uniform distribution. In each period the high bidder earns a profit equal to his or her value less the auction price; other bidders earn zero profit. Bids are commonly restricted to be nonnegative and rounded to the nearest penny. Theory does not specify what information feedback bidders get after each auction, which usually differs between experimenters and which will be shown to impact bidding. At the time of the 1995 survey, it was clear that both the RET as well as the strategic equivalence between English and second-price and Dutch and first-price auctions failed. Further, there were persistent reports of significant bidding above the riskneutral Nash equilibrium (RNNE) benchmark in FPSB auctions, initial explanations of which focused on risk aversion. This explanation generated considerable controversy among experimenters (see the December 1992 issue of the American Economic Review). Sorting out between explanations for bidding above the RNNE in FPSB auctions has preoccupied a number of later papers as well, several of which are reviewed first.

1.1 Bidding above the RNNE in First-Price Private Value Auctions Isaac and James (2000a) compare estimates of risk preferences from FPSB auctions to the Becker-DeGroot-Marshak (BDM) procedure for comparably risky choices.2 Aggregate measures of risk preferences under the two procedures showed that bidders were risk averse (RA) in the FPSB auction but risk neutral, or moderately risk loving, under the BDM procedure. Further, looking at individual subject measures of risk preference between the two procedures (see Figure 9.1), there is a modest negative relationship between the two, indicating those counted as most RA in FPSB auctions, tend to be least RA under BDM. Although it is well known from the psychology literature that different elicitation procedures commonly yield somewhat different quantitative responses (see Camerer 1995, 657–61; Mellers and Cooke 1996), a negative relationship between the two measures is not what one would expect. Under the circumstances, while one can still maintain a hypothesis of RA in the FPSB auctions, an equally compelling alternative hypothesis is confusion of one sort or another in the FPSB auctions and/or confusion with respect to the BDM procedures.3 Dorsey and Razzolini (DR; 2003) look at IPV auctions in which a single human bidder competes in a series of FPSB auctions with three simulated buyers who bid according to the RNNE. They compare bids in this setting to an equivalent lottery procedure in which the same subjects essentially pick their preferred probability of winning against their computerized rivals, with expected profits conditional on winning being computed for them for each probability level chosen. Mean lottery-equivalent bids are compared to mean auction bids over the relevant range of valuations. As shown in Figure 9.2, mean bids are essentially the same between the two procedures over the interval [0, 750], the first three quarters of the uniform distribution from

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Figure 9.1: Modest negative relationship between different risk measures.

which valuations were drawn. In the remaining interval the lottery equivalent bids are consistently lower than the auction bids, suggesting that probability miscalculations (how close rivals’ valuations are to your own) play some role in bidding above the RNNE at higher valuations. DR also compared bids in FPSB auctions, where subjects are told the probability of winning the auction for each possible valuation, with the lottery equivalent procedure. In this case bids under the two procedures overlapped over the entire range of valuations, which supports their probability miscalculation hypothesis. Finally, note in Figure 9.2 the humped-back nature of the deviations from the RNNE over the range of possible valuations, with mean bids essentially equal to the RNNE over lower valuations, above the RNNE (with the difference growing) for middle valuations, and falling below the RNNE (and differing substantially) at the highest valuations. We will return to this point later. Armantier and Treich (2009), employing similar manipulations, reach even stronger conclusions that biased probabilistic beliefs are the primary driving force behind bidding above the RNNE, with risk aversion playing a lesser role than previously believed.4 Neugebauer and Selten (NS; 2006) compare different information feedback treatments in a series of FPSB auctions against computerized rivals. They focus on three types of information feedback: (1) no information about bids of computerized rivals, just telling bidders if they won the auction or not, along with profits earned if they won, (2) adding information about the bid of the highest computerized rival when they did not win (i.e., the market price, which is the feedback usually employed in experiments), and (3) adding information about the highest computer’s bid in case of winning the auction. They look at differences between actual bids and the RNNE bid in the first auction period and averaged over the entire set of 100 auctions, and do this with different numbers of computerized rivals. The number of subjects bidding above the RNNE in the first auction period is reasonably small under all three treatments— 22%—with minimal differences between the three treatments. However, averaged over all auctions, there was significant movement towards bidding above the RNNE in all

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three treatments, with the largest increase in treatment 2; 75% of all subjects bidding above the RNNE, with a constant relative rate of risk aversion (r i ) of 0.78.5 In contrast, under treatments 1 and 3, 41% and 48% of subjects bid above the RNNE, with an average estimated r of 1.25 and 1.17, respectively (i.e., on average subjects act as if they are risk loving). NS use “learning direction theory” to explain the changes in bidding over time under the different feedback conditions.6 Goeree, Holt, and Palfrey (GHP; 2002) report a series of FPSB auctions with two bidders with a limited number (6) of discrete values (requiring discrete bids as well). They employ a low- and high-value treatment with the same RNNE bid in both treatments but with the cost of bidding above (below) the RNNE being higher in the low- (high-) values treatment. Discrete values are employed in order to estimate a quantal response equilibrium (QRE). They find bidding above the RNNE in both treatments, with an estimated constant relative risk aversion (CRRA) under the QRE of approximately 0.50 in both cases. They compare their QRE model with risk aversion to (1) a nonlinear probability-weighting model and (2) a joy-of-winning model. The nonlinear probability-weighting model fits the data as well as the QRE with risk aversion but has one additional parameter and does not overweight (underweight) small (large) probabilities, as one would expect. Joy of winning adds nothing to the QRE estimates with risk aversion, while a pure joy-of-winning model fits the pooled data quite well, although not as well as the QRE with risk aversion. GHP take on the Rabin (2000) critique that estimates of risk aversion from laboratory experiments do not plausibly scale up to larger gambles, as given the levels of risk aversion reported, subjects would (implausibly) avoid very attractive large gambles. Their response to this critique is that the relevant argument in subjects’ utility function is gains and losses from particular gambles and/or is defined over a smaller time interval (e.g., within the experimental session itself), as opposed to changes in wealth. On this point, also see Cox and Sadiraj (2006). Cason (1995) investigates SB emission-trading auctions where both constant absolute risk aversion and CRRA require bidding below the RNNE. In auctions with all human bidders, 75% of the subjects bid above the RNNE. Replacing the human competitors with robots, the number of subjects consistently bidding above the RNNE dropped to 50%.7

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1.2 Bidding above the RNNE and Regret Theory Rabin (2000) points out that alternatives to expected utility theory would seem to provide a more plausible account of the substantial risk aversion over modest stakes observed in experiments without requiring ridiculous levels of risk aversion over large stakes. Filiz and Ozbay (FO; 2007) explore the implications of one such model, regret theory (Loomes and Sugden 1982; Bell 1982) in an experiment looking at bidding in FPSB auctions.8 In their analysis they note that the information bidders receive at the end of the auction may generate one of two types of regret: (1) “loser’s regret” if a losing bidder could have won the item with a higher bid and earned positive profit and (2) “winner’s regret” if a winning bidder could have earned more by bidding less (money left on the table). They first demonstrate that loser’s regret by itself will generate bidding above the RNNE and that winner’s regret, by itself, will generate bidding below the RNNE. To isolate the effect of these two factors and to judge their relative strength, they conduct a series of one-shot, FPSB auctions in which, following completion of the auction, (1) losers learn the winning bid but the winner learns nothing about others’ bids (loser’s regret), (2) winners learn the second-highest bid but losers learn nothing about the winner’s bid (winner’s regret), and (3) a control treatment in which bidders learn nothing about others’ bids (no regret). They run one-shot, as opposed to repeated, auctions on the grounds that their theory relies on bidders anticipating future regret in terms of their current decisions, while repeated auctions introduce the possibility of regret from outcomes in previous auctions. To gather sufficient data, they solicit bids for 10 possible valuations from each bidder, and use the average bid (across bidders) at each of these valuations as the dependent variable in estimating linear bid functions with four bidders in each auction.9 The estimated slope of the bid function in the control treatment (no information provided) is 0.79, just within the 95% confidence interval for the RNNE value of 0.75 in auctions with four bidders. The slope estimated from the winner’s regret treatment is just below this (0.77) but is not significantly different from the no information treatment. However, the slope of the loser’s regret treatment is 0.87, which is significantly higher than the no information treatment. Although averaging bids across subjects with the same valuations does not bias the estimated slope coefficients, it no doubt biases the standard errors of the estimates downward as it removes any between-subject variation in bids. Thus, the statistical significance of their results is suspect.10 Engelbrecht-Wiggans and Katok (EK; 2008, 2009) report two experimental investigations of regret theory with human bidders competing against two computerized rivals. The primary variation between the two papers consists of the number of auctions bidders receive feedback from. When subjects receive feedback on 1,000 auctions evenly divided between each of 5 valuations, the predictions from regret theory are supported across the board, although it takes some time before bidding under winner’s regret drops below no regret (no feedback, Engelbrecht-Wiggans and Katok 2008). Results are considerably more mixed when subjects decisions affect only a single auction and they only receive feedback for that one auction (Engelbrecht-Wiggans and Katok 2009).11 The NS experiment discussed in Section 1.1 also has implications for regret theory as their treatment 1 corresponds to a no regret treatment, with treatment 2 corresponding to FO’s loser’s regret. For bidders competing against three or four computer rivals (the treatments that come closest to FO and EK), NS find 50% of their subjects bidding above the RNNE in the first auction of their no-regret treatment versus 9.1% in their loser’s regret treatment, which does not match FO’s results. Averaged over all auctions they

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find essentially the same number of subjects bidding above the RNNE in the no-regret and loser-regret treatments, which is qualitatively consistent with EK (2009). To sum up: The design and execution of experiments to explain bidding above the RNNE in FPSB auctions on account of regret theory is quite innovative. However, the statistical significance of FO’s results are suspect, NS fails to replicate their results, and EK’s results suggest that the impact of regret is sensitive to the level of feedback subjects get regarding auction outcomes.12 Nevertheless, the idea that loser’s regret is greater than winner’s regret receives support from studies showing that subjects tend to increase their bid-to-value ratio more often in response to losing out on an income earning opportunity compared to leaving money on the table (Ockenfels and Selten 2005; Cason and Friedman 1997, 1999). One important methodological point these experiments emphasize is that results from earlier experiments can be, and often are, reinterpreted in light of new and different theoretical perspectives. This, in turn, calls for new experiments to see if the insights from the new perspective are satisfied in the data. On this score there is still more work to be done on anticipated regret if it is to explain bidding in private value auctions.13 1.3 Using Experimental Data to Corroborate Maintained Hypotheses in Empirical Applications to Field Data Bajari and Hortacsu (BH; 2005) use experimental data from FPSB auctions with three and six bidders to nonparametrically estimate bid functions. The primary purpose of their paper is to determine whether structural models of first-price auctions as applied to field data can generate reasonable estimates of bidders’ private information.14 The latter is an essential element of what econometricians hope to recover in examining field data. In using experimental data, the econometricians have at their disposal bidders’ actual valuations against which to judge the accuracy of the recovery process, data that are not available in field applications. Further, unlike with field data, there is no question that one is dealing with an IPV auction, as opposed to a common value or affiliated private value auction, which reduces the possibility of specification errors. The results are also of interest to experimenters as BH test between four competing models: (1) the RNNE, (2) Nash equilibrium bidding but with (homogenous) CRRA bidders, (3) an adaptive learning model in which bidders maximize their expected utility based on beliefs about the distribution of bids (formed on the basis of previous auction outcomes), and (4) QRE with CRRA bidders. Their results show that Nash bidding with risk aversion provides the best overall fit to the data.15 Further, they are unable to reject a null hypothesis that the actual and estimated distribution of bidder valuations is the same under this specification. In reaching this last conclusion they need to trim the upper bound of the support from which valuations are drawn (corresponding to the top 5% of all bids) as there is a negative correlation between bids and values over this part of the support. This is consistent with DR’s results, reported in Section 1.1, that at the highest private valuations bids actually drop below the RNNE reference point. QRE with risk aversion provides results similar to those of the Nash model with risk aversion, but does not correctly pin down the lower end of the support from which valuations are drawn. In short, this whole exercise represents a novel use of experimental data. It also illustrates the potential for complementarities between experimental and “real” data. On this score, also see Sections 1.7 and 2.5.3 for applications of applied econometric techniques employed in analyzing field data to better understand experimental outcomes.

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1.4 Second-Price Private Value Auctions The 1995 survey covered research showing a breakdown in the strategic equivalence between second-price and English clock auctions, primarily as a result of bidding above value in second-price auctions as opposed to sincere bidding (bids equal to value) in the clock auctions. Since then there have been several experiments designed to better understand why subjects overbid in second-price auctions, as well as why subjects do so much better in English clock auctions. We review these next. Shogren, Parkhurst, and McIntosh (SPM; 2006) report bids from SPSB auctions conducted under a tournament structure so that bidder earnings depend on the total points earned over 20 auction trials: the player with the most total points earned $120, the second most earned $80, and so on, with the three lowest earning $5 each. They compare bidding in the tournament to bidding in a series of 20 standard SPSB auctions. Each auction had a total of 10 bidders, who were repeatedly matched with each other as part of the tournament structure.16 Deviations from sincere bidding were much smaller in the tournament than in the standard SPSB auctions, with the difference between bids and values (bid − value) averaging 6.28 (63.51) points in the standard auctions versus 0.96 (4.14) in the tournament (standard deviations are in parentheses). However, there were relatively small differences in the frequency with which the highest value bidder won the auction averaging 55.0% in the tournament versus 42.5% in the standard auctions, with similar results for the frequency with either the highest or second-highest-value bidders won (72.5% in the tournament versus 70.0% in the standard auctions). SPM conjecture that the superior performance in the tournaments results from the fact that the typical mistake of bidding above value has a much greater adverse effect on outcomes given the tournament pay structure. Although these results are interesting and consistent with their hypothesis, their analysis ignores the fact that in a tournament deviating from sincere bidding may be optimal.17 Garratt , Walker, and Wooders (GWW; 2012) conduct a SPSB auction using subjects who regularly participate in eBay auctions for Morgan (“Golden Age”) silver dollars. Arguably, these subjects have considerable field experience given the similarity between eBay and second-price auctions. (But there are significant differences; see Roth and Ockenfels (2002), reported in Section 4.3.) GWW invited these bidders to participate in a standard SPSB auction with induced valuations from a support comparable to the range of values that Morgan silver dollars sell for. There were 5 bidders in each auction. After bidding once in a presumably one-shot auction, subjects were invited back for a second round of bids, conducted as a control against possible skepticism that payoffs in round 1 might not be for “real.” Figure 9.3 shows bids and valuations from their experiment. Looking at these, GWW conclude that “despite having substantial experience with auctions in the field, eBay subjects do not value bid.” They compare the frequency of sincere bidding to Kagel and Levin’s (KL; 1993) experiment, employing the same criteria that any bid within five cents of a subject’s value is counted as sincere. They find essentially the same frequency of sincere bidding, 21.2% versus 27.0% in KL. However, there is substantially more underbidding than overbidding in their data: 41.3% (37.5%) underbidding (overbidding) in GWW versus 5.7% (67.2%) in KL. GWW are able, at least qualitatively, to resolve this discrepancy after they break their data down into eBay-only buyers versus eBay-sometime sellers, as sellers tend to underbid much more often than buyers (50.9% versus 29.5%). There is a corresponding discrepancy in the

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frequency of overbidding, 45.5% for buyers versus 32.1% for sellers, with both sets of differences statistically significant at the 10% level using a nonparametric MannWhitney test.18 The fact that frequent sellers underbid, as opposed to those with no selling experience tending to overbid, has certain parallels to Burns’ (1985) study comparing professional wool buyers to students in a continuous double-auction market. In that experiment the students performed much better than the wool buyers (earning more money with more efficient outcomes), in large measure because the wool buyers ignored subtle differences between the laboratory experiment and the wool market. The connection here is that people who sell on eBay will typically buy only if the price is below their value, as otherwise they cannot profit from resale, and one cannot expect them to ignore these habits when put into a new situation. This is consistent with the psychology literature, which suggests that in deductive-reasoning processes people typically employ shortcuts, developing mental models of situations and reasoning about them in the context of the model (Johnson-Laird 1999). Thus, it is easy to see how Burns’ wool buyers might behave in ways that are more appropriate to their customary environment, which was similar to, but not exactly the same as, the laboratory environment. Similarly, it is easy to see how eBay sellers, who make a living by buying low and selling high, might deviate from sincere bidding by bidding less than their induced values, while buyers, as is typical of standard laboratory subjects, bid above their induced values. In short, there is no particular reason to think that experienced professionals will perform much better than student subjects when placed in a laboratory setting, unless there are strong and relevant similarities between the field setting they are familiar with and the laboratory environment.19 Andreoni, Che, and Kim (ACK; 2007) report the highest rate of sincere bidding in SPSB auctions we are aware of—77.3% overall (85.5% in the last 10 periods)— in auctions with 4 bidders and a uniform distribution of valuations. They find that

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sincere bidding drops substantially, largely replaced by overbidding, when subjects know their rivals resale values. They attribute this result to spite.20 While spite might explain overbidding when rivals valuations are known, this does not provide a credible explanation for overbidding absent this information, as there is minimal overbidding in English clock auctions, which are strategically equivalent and in which spite (as well as joy of winning) should play just as strong a role. Cooper and Fang (CF; 2008) look at bidding in a series of 2-player second-price auctions with bidders valuations drawn from an approximate normal distribution. Their primary treatment variable consists of noisy information about rival’s valuations, which in some cases is provided exogenously and in other cases can be purchased. In the control treatment, with no information about rival’s valuations, just under 40% of all bids are sincere, with overbidding accounting for most of the deviations. Unlike ACK, with exogenously provided information about rival’s valuations, the rate of sincere bidding increases, especially with less noisy information. The probability of overbidding is reduced in response to costly mistakes (overbidding that causes subjects to lose money), with the apparent stability of bidding above value resulting from the infrequency of costly mistakes. CF also find that subjects tend to buy costly information about rivals’ valuations (since the game has a dominant strategy; at least from a game-theoretic perspective, this involves throwing money away), with these purchases diminishing over time. There is considerable heterogeneity in these purchases, with subjects who overbid the most buying information more often. This suggests a split in the population between more “rational” types, who neither overbid nor pay to buy essentially worthless information, and less rational types, who commit both types of mistakes. Georganas, Levin, and McGee (2010) look at the effect of penalties for deviations from sincere bidding. This involves multiplying any realized losses by a factor β, where β is at times greater than 1, equal to 1, or less than 1. These penalties have no impact on the dominant strategy. Although subjects fail to discover the dominant strategy, they respond “sensibly” to changes in the value of β, getting closer to the sincere bidding when β = 20, and further away when β = 0.1 (see Figure 9.4). The impact of the change in β is immediate and occurs even though bidders do not typically lose money when deviating from sincere bidding. These responses are consistent with the notion that subjects bid above value in SPSB auctions out of the mistaken notion that it increases the likelihood of winning with minimal adverse income effects, as winners pay the second-highest bid (see Kagel, Harstad, and Levin 1987). In terms of this argument, what changing β does is to alter the potential cost of such wins, which in turn alters bids in the expected direction. Although joy of winning can also explain bidding above value (with changes in β impacting the cost of doing so), joy still cannot explain why bidding above value is so limited in standard English clock auctions and so prevalent in SPSB auctions. 1.5 Asymmetric Private Value Auctions While much of the auction literature has focused on bidders that are ex ante symmetric, in many auctions it is commonly known that one or more bidders (the strong bidders) are likely to have higher valuations for the auctioned item than the other (weak) bidders. This extension of the private values model raises interesting theoretical questions (see Maskin and Riley 2000) that have been explored in a handful of experimental studies.

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Pezanis-Christou (2002) investigates a model with two risk-neutral bidders (i = 1, 2) each demanding a single unit. Bidders’ values are independent draws from a uniform distribution, with support [0, 100] for the strong bidder and support [−100, 100] or [−300, 100] for the weak bidder, so that the underlying support for the strong bidder first-order stochastically dominates (FOSD) the weak bidder. Negative bids are not allowed, with the weak bidder not allowed to bid when receiving a negative value. Each session consisted of either 60 or 72 auctions in which subjects’ type change between auctions, along with changes in the support for weak bidders’ values. FPSB and SPSB auctions were run. Key comparative static predictions investigated are: (1) In the FPSB auctions the strong types bid less aggressively than weak types for the same private valuation; (2) efficiency is greater in the SPSB auctions; and (3) expected revenue is higher in the SPSB auctions. The intuition underlying (3) is that since there is a positive probability that the weak bidder will not bid (as a result of a negative value), strong bidders in the FPSB auctions maximize their expected earnings by placing very low bids (“low balling”) when they get low values. In contrast, sincere bidding remains a dominant strategy in the SPSB auction, resulting in higher revenue on average. Both the frequency of low-balling and the revenue differences should be greater when the weak bidder has a greater likelihood of drawing a negative value (with support [−300, 100]). As predicted, strong bidders shave their bids more than weak bidders do in the FPSB auctions under both treatments, where bid shaving is defined as the ratio εi = (vi − bi )/vi , where vi is bidder i ’s value. And they shave more when weak bidders’ draws are from [−300, 100]. About 46% of all second-price bids were sincere, with 40% of bids above value. SPSB revenues were close to their predicted level, indicating that whatever overbidding there was had to be relatively small. As predicted, the SPSB auctions have higher efficiency, averaging 97% versus 95%, with weak bidders’ support [−100, 100] and 99% versus 96% with support [−300, 100].21 However, contrary to the theory, average revenue was greater in the FPSB auctions in both cases. Although average revenue in the SPSB auctions was approximately

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equal to its predicted value, revenue in the FPSB auctions was well above the RNNE prediction. Pezanis-Christou attributes this failure of the theory to bidders’ difficulty in recognizing the profitable opportunities from low-balling in the FPSB auctions. However, he does not attribute this to risk aversion as (1) with the weak bidders’ draws from the interval [−300, 100], the revenue ranking is not affected by risk aversion, (2) simulations assuming both bidders are extremely risk averse cannot account for the reversal of the revenue ranking with weak bidders’ draws from the interval [−100, 100], and (3) the extent to which strong types bid above the RNNE in the FPSB auctions was decreasing over time, suggesting that subjects were employing an adaptive bidding strategy, as opposed to a static, fully optimizing one.22 Güth, Ivanova-Stenzel, and Wolfstetter (GISW; 2005) conduct an experiment in which bidders’ values were drawn from a uniform distribution with support [50, 150] for weak types versus [50, 200] for strong types, running both first- and second-price sealedbid auctions. As predicted under the RNNE, efficiency is consistently higher in the SPSB auctions, averaging 98%, 99%, and 99% versus 97%, 97%, and 98% over the 3 phases of the experiment.23 Although the theory predicts that weak bidders’ payoffs will be higher in the FPSB auctions and strong bidders’ payoffs higher in the SPSB auctions, both types’ average payoffs are significantly higher in SPSB auctions. Bids are close to predicted levels in the SPSB auctions (sincere bidding), but as typically reported, are substantially higher than the RNNE in the FPSB auctions. The latter accounts for the failure of weak bidders’ payoffs to be higher in FPSB auctions. A closer look at bid patterns shows that strong bidders in FPSB auctions generally obey first-order rationality because there are few bids above 150, the maximum possible valuation for weak bidders. Further, weak bidders shave their bids less than strong bidders at higher valuations (v ≈ 100). Although this satisfies a key qualitative prediction of the theory, the pattern differs from the predicted one as the differences in bid shaving between weak and strong bidders does not increase monotonically over higher valuations, and the differences are not nearly as large as the theory predicts. When given a choice, both weak and strong bidders overwhelming chose the second-price auction, consistent with the significantly higher payoffs for both types under this format. Chernomaz (2012) studies asymmetries resulting from two otherwise symmetric bidders merging to submit a single bid based on the highest of their private valuations.24 This strong bidder competes against a single weak bidder. Each bidder draws a private value from a common uniform distribution, but by virtue of using the higher of their 2 private values, the value distribution for the strong bidder FOSD the weak bidder. Subjects participate in a series of FPSB auctions under each of three treatments: (1) They bid as separate entities based on their private values in an auction with three bidders. (2) “Merged” firms let each subject bid separately, with no communication, based on the higher of their two valuations. (3) Merged firms submit a single agreed-upon bid after they have the opportunity to communicate via an instant messaging system. Subjects’ roles as weak or strong bidders remain fixed throughout a session, as do the pairings for the “merged” firm. The dual-market technique is employed so that in each auction bids under all 3 treatments are based on the same valuations, with the market to be paid off on determined randomly. Between-treatment predictions consist of the following: In equilibrium, the strong type bids less than the weak type with the same valuation, resulting in less efficient allocations compared to the symmetric (3-bidder) auctions. Following the “merger,” both weak and strong types bid lower than in the symmetric (3-bidder) auctions. As a result, revenue decreases and bidders’ profits increase, with the weak bidder getting a

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larger absolute increase than the strong bidders after splitting their earnings. This last result has implications for the incentive to merge and bid jointly in a fully blown model where joint bidding is determined endogenously.25 The experimental results show bidding above the RNNE in both the symmetric and asymmetric auctions. Strong types bid less aggressively than in the symmetric auctions, although the difference is not as large as the theory predicts. Weak types bid the same, or slightly higher, than in the symmetric auctions. Chernomaz shows that this difference can be partly accounted for by the greater incentive strong types have to reduce bids. Contrary to the RNNE prediction, efficiency is higher with joint bidding than in the symmetric benchmark case. This can be explained by the reduction from three to two bidders, so that any inherent noise in bids is less disruptive to efficiency in the 2-bidder case, as bidders’ valuations are further apart on average than in the 3-bidder case.26 Strong bidders benefit from joint bidding at least as much as the weak bidders (even after accounting for splitting their profits), indicating that the incentive to bid jointly is stronger than predicted. Finally, there are essentially no differences in bids when members of the “merged” firm bid individually versus bidding jointly. But for some unknown reason, weak bidders tend to submit higher bids when the “merged” firm bids jointly. Goeree and Offerman (GO; 2004) explore the revenue-raising properties of the Amsterdam auction when bidders have asymmetric valuations.27 The Amsterdam auction has two stages: Stage 1 consists of an English clock auction until all but two bidders have dropped out. The price at which the last bidder dropped out is called the bottom price and serves as a reserve price in stage two. Stage 2 consists of either a first- or second-price sealed-bid auction. Further, and this is the unique element, in the second phase both bidders receive a premium, which is a proportion of the difference between the lowest stage 2 bid and the bottom price. With asymmetric valuations, the Amsterdam auction provides endogenously determined incentives for weak bidders to compete against stronger rivals. GO compare both a FPSB and SPSB Amsterdam auction with a standard FPSB, an English clock auction and Myerson’s (1981) optimal auction design. Treatments consist of symmetric valuations and weakly asymmetric and strongly asymmetric valuations, with four bidders in all auctions (three weak and one strong bidder in the asymmetric auctions). The standard FPSB auction generates significantly more revenue than the other auction formats with symmetric valuations (including the optimal auction) as subjects bid well above the RNNE.28 In the weakly asymmetric case the FPSB, the Amsterdam first-price and the optimal auction all raise significantly more revenue than the other two formats (with the FPSB ahead by a nose). In the strongly asymmetric case, the Amsterdam auction raises significantly more revenue than the FPSB and the English auction, with the Amsterdam second-price auction raising 10% more revenue than the first-price Amsterdam auction and only slightly less revenue (7%) than the optimal auction. English auctions consistently have the highest efficiency but with strong asymmetries, absent some sort of positive incentives for weak bidders, this strongly discourages participation as weak bidders (correctly) anticipate that they have little chance of winning (Klemperer 2002).29 Summing Up. Tests of revenue predictions in asymmetric private value auctions are confounded by the fact that subjects tend to bid well above the RNNE in FPSB auctions, but bid close to the dominant strategy in SPSB auctions with only two bidders. Bid functions tend to move in the right direction, at least qualitatively; strong bidders tend to bid less than weak bidders for comparable valuations in FPSB auctions. Efficiency

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tends to be lower in FPSB compared to SPSB auctions, which is the same result reported for symmetric FPSB and SPSB auctions (reviewed in Kagel, 1995). One secondary result of these experiments is that they show closer conformity to sincere bidding in SPSB auctions with two bidders than typically found with larger numbers of bidders. With strong asymmetries, the Amsterdam auction raises more revenue than a FPSB auction and generates almost as much revenue as Myerson’s optimal auction design, but it requires much less information on the part of the auctioneer than the optimal auction.30 1.6 Sequential Auctions Experimental research on single-unit-demand sequential auctions has been devoted to exploring the declining-price anomaly reported in field data: prices of homogenous auctioned items decrease systematically over the course of selling multiple items (Ashenfelter 1989; Ashenfelter and Genesove 1992). Declining prices are an anomaly because economic intuition suggests that prices of identical items sold in a sequence at the same time and place should be the same when each bidder demands a single item. Weber (1983) proves this to be the case for risk-neutral bidders. Further, although intuition suggests that risk aversion may cause prices to decline, McAfee and Vincent (1993) demonstrate that this can be guaranteed only if buyers have strictly increasing absolute risk aversion, a questionable assumption. One advantage of controlled laboratory experiments on this topic is that one can ensure that bidders have single-unit demands, which is not assured when looking at field data. This is important since with multiple unit demands, there are circumstances under which decreasing prices would be expected to occur. Keser and Olson (KO; 1996) report the first sequential-auction experiment with unit demands with paid subjects.31 Each auction consisted of 8 bidders with a known supply of 4 units, bidding in a sequence of FPSB auctions. Each bidder made a bid for the first unit, with the highest bidder receiving that unit at the price bid. The winning bidder was no longer permitted to bid, with the auction continuing with new bids solicited for a second unit, and so on, for all 4 units. Prices of units sold were announced following the sale of each unit. Values were iid from a uniform distribution. Four sessions with 20 auction periods each were conducted, with subjects not permitted to bid above their values. The symmetric RNNE bid function for unit l under this design with support [0, 1] is

bl (ν) =

n−k (ν ) n − l −1

where v is the bidder’s valuation, n is the number of bidders, and k is the number of units sold, so that bids on later units are substantially closer to bidders’ values than earlier units. However, expected prices remain constant as bidders with higher values get units earlier than those with lower values. Table 9.1 reports realized and predicted prices for each of the four units. There is some variation in predicted prices as a consequence of the random draws used in the experiment. Both average and median realized prices decline for later units, consistent with the declining-price anomaly. Further, prices were higher than the RNNE for all 4 units, only more so for early units. Overall, average efficiency was 98% compared to close to 85%, based on randomly allocating units among the 6 highest-value bidders.

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TABLE 9.1: Realized and predicted prices: first-price sequential auctions.

Predicteda average (std) Realized Mean (std) Median

Unit 1

Unit 2

Unit 3

Unit 4

444 (41)

446 (80)

449 (100)

426 (133)

500 (104)

474 (76)

463 (70)

454 (121)

492

470

461

456

Notes: a Based on bidders’ realized valuations; std = standard deviations. Source: Keser and Olson (1996).

Bidding was consistently above the RNNE benchmark, so that one might suspect that heterogeneous risk preferences, or regret theory, could help resolve the declining-price anomaly.32 We are aware of two replications of the KO experiment. Salmon and Wilson (2008) report an experiment in which 2 units were sold sequentially in auctions with 4 bidders using an English clock procedure. This was used as a control treatment for the secondchance offer auctions discussed in Section 4.3. They report average prices of 335 for the first unit sold versus 273 for the second, compared to the equilibrium prediction of 270 for both units. Neugebauer and Pezanis-Christou (NPC; 2007) report a series of FPSB sequential auctions with 8 bidders and 4 units supplied. Values were iid from a uniform distribution with support [0, 100], with winning prices announced following each unit sold. One major difference from the KO experiment is the number of auctions in a session—100 here as opposed to 20 in KO.33 NPC measure efficiency in terms of the proportion of allocations to bidders whose value ranking was lower than the order in which units were offered—yielding an average aggregate efficiency of 72%. Misallocations were greater for units 1 and 2 than for 3 and 4, indicating that the highest-value bidders had adopted a “wait-and-see” strategy regarding sales of early units, giving bidders with lower values a chance to win these early units. One consequence of this is that average prices were approximately constant across units, ranging from a high of 51.7 on unit 1 to a low of 49.5 on the unit 4. So, in this case the “right” result for prices is achieved for the wrong reason—systematic deviations from the predicted order in which units were sold, with lower-valued bidders tending to buy earlier units. One side note here: Like KO, average prices were decreasing across units in the first 20 auctions in NPC, the total number of auctions in KO’s sessions, as it took some experience for higher-valued bidders to learn the benefits of the wait-and-see strategy. Summary. Multiple-unit sequential auctions typically exhibit the decreasing price anomaly observed in field settings. Observing decreasing prices in the laboratory suggests that the field outcomes cannot be solely attributed to supply or value uncertainty, the presence of buyers’ agents in the bidding pool, or other factors that may contribute to the phenomena in less-structured field settings. These results establish an important connection between laboratory and field settings. What’s missing with respect to this line of research are direct comparisons of single-unit sequential auctions with, for example, simultaneous or uniform price auctions in terms of the relative impact on

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revenue and efficiency in order to get some idea of which auction mechanism is likely to perform best in field settings. 1.7 Procurement Auctions In procurement auctions the lowest bid wins, but this is not the reason to have a separate section from the buyers’ bid auctions (high bid wins). Rather, there are a number of issues peculiar to business-to-business (B2B) auctions. In particular “quality” becomes an important issue. In some cases buyer-determined auctions are nonbinding because the buyer does not commit to award the contract to the lowest bidder. Rather, the buyer reserves the right to select the winner based on bid (price) and “quality.” Quality is typically treated as exogenous and consists of factors that cannot be easily quantified, such as reputation and past relationships, so that no explicit scoring rule is announced in advance.34 Research on these types of auctions, which are quite common for firms purchasing goods and services in B2B auctions (Jap 2002), is just beginning. Engelbrecht-Wiggans, Haruvy, and Katok (EWHK; 2007) address the question of under what circumstances a buyer-determined (BD) mechanism increases the buyer’s surplus, as opposed to a price-determined (PD) mechanism, where the buyer commits to awarding the contract to the lowest bidder. They consider an IPV auction in which quality Q = C + γ X, where C (cost) is uniformly distributed on (0, 100), X is uniformly distributed on (0, 1), and γ is a constant, so that C and Q are positively correlated. This specification turns a 2-dimensional problem in terms of seller’s costs and quality into a 1-dimensional problem in which each seller knows his or her own Q i , as do buyers, prior to the start of the auction. Each seller bids a price B(C i , Q i ), with the buyer selecting the seller with the highest score Q i − B(C i , Q i ). Under the RNNE, FPSB and SPSB auctions generate the same expected buyer surplus, with the superiority of the buyerdetermined mechanism varying as a function of the number of competitors (N) and the extent to which cost is correlated with quality (γ ). Three treatments are studied: (1) N = 2 and γ = 100, so that average buyers’ surplus is greater under the buyerdetermined mechanism, (2) N = 2 and γ = 300, so that buyers’ surplus is greater with the price-determined mechanism, and (3) N = 4 and γ = 300, so that average buyers’ surplus is greater under a buyer-determined mechanism. FPSB auctions are employed throughout. Aggregate results comparing buyer surplus confirm these comparative static predictions, with stronger results for experienced than inexperienced bidders. Efficiency, defined as the frequency with which the highest-scoring bidder wins the auction, is consistently higher under BD than under PD, but consistently lower than the point prediction under BD (between 81% and 89% versus 100% predicted). One important shortcoming of this experiment relative to the target environment is that both buyers and sellers know Q i with certainty prior to the start of the auction, which is almost certainly not the case in most field settings. There are, however, problems in establishing clear analytic predictions when Q i is uncertain or is not known by other bidders. Nevertheless, both the analytic and experimental results serve to disabuse practitioners of the common notion that buyer-determined auctions will always give them the best of both possible worlds: the intense price-based competition of price-based auctions and the ability to account for subjective quality characteristics, as in more traditional approaches to procurement. Haruvy and Katok (HK; 2013) consider BD auctions with and without information about other bidders’ quality, using both FPSB and English auctions. They use the same

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experimental setup as in EWHK, focusing on the treatment with γ = 300 and N = 4. With full information, each bidder knows all other bidder’s qualities (Q) as well as whether his or her own Q is the highest. Under private information bidders know only their own Q. Given the IPV assumption, under the RNNE expected buyer surplus is the same under full information in the English auction and with private information in the FPSB auction. Further, as with standard English auctions, bidders have a dominant strategy to bid down to their cost of production before exiting the auction. Analytic results are not available for English auctions with private information regarding Q or in FPSB auctions with full information regarding Q. However, numerical analysis based on linear approximations of the relevant bid functions, and the draws employed in the experiment, show that: (1) efficiency is lowest in the FPSB auctions with full information, near 100% in the English auctions with private information, and 100% in the other two cases, and (2) predicted buyer surplus is lowest in the English auction with private information regarding Q and highest under the FPSB auction with full information, with expected surplus under the other two treatments falling approximately halfway between the other two cases. Results show that realized buyer surplus is quite close to predicted surplus in the English auctions with full information but significantly higher than predicted in the other three treatments, with the highest surplus achieved in the FPSB auction with private information. The latter corresponds to the standard FPSB auction result in which bids typically exceed the RNNE (in this case, are below the RNNE), so that buyer surplus is higher in the FPSB auctions. Actual buyer surplus under English auctions with private information about quality is significantly higher than under English auctions with public information about quality. This provides support for the idea that English auctions with information on bid ranks often employed in BD auctions, as opposed to precise bid information, is surplus enhancing.35 Efficiency however is in the mid-80s in all four treatments, with little difference between any of the four cases.36 In BD auctions, it is not uncommon for buyers to have an incumbent supplier competing with a potential new supplier where there is uncertainty whether or not the latter will qualify after the auction ends. Wan, Beil, and Katok (WBK; 2012) investigate a stylized model of this sort. In their main treatment condition, the buyer conducts a descending-price English auction between the entrant and the incumbent without prequalifying the entrant. The focus is on incumbents under conditions where if the entrant wins but does not pass qualifying after winning the auction, the incumbent wins at the price at which they dropped. This sets up a type of asymmetric auction where the potential entrant bids down to their supply cost and the incumbent games the fact that there is uncertainty regarding the potential entrant’s ability to meet qualifications. Depending on the incumbents supply cost, he or she follows one of three strategies: (1) boycott the auction, bidding the reserve price and no lower, (2) bid to win, dropping out only when the price hits their costs, and (3) “testing the water,” hoping to win the auction on price alone but not competing down to costs. Boycotting is employed when the incumbent knows he or she is unlikely to beat the entrant on price alone. Low-cost incumbents employ a bid-to-win strategy, competing down to their costs. Moderate-cost incumbents employ a mixture of the two strategies, dropping out before price reaches their costs, relying on the fact that the entrant might not qualify after the auction ends. Since entrants have a dominant strategy to compete down to their cost, to simplify the experiment, the computer plays the role of the entrant. Parameter values are set at a low (30%) or high (70%) probability the entrant will qualify, with the incumbent having slightly higher potential costs than the entrant. The reserve price is set at the upper

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bound of the support for the incumbent’s cost. Point predictions assume risk neutrality for the incumbent. The data show that incumbents fail to use optimal threshold strategies for when to drop out, so WBK focus on whether the qualitative predictions of the model are satisfied. Incumbents are found to be more likely to boycott, the higher their costs, with a relatively high percentage of boycotting (40% to 80%) under parameter values where they should boycott regardless of costs. For parameter values where the incumbent should bid to win, the lower their costs the more likely they are to do so. With “testingthe-water” parameter values, on average bids are lower than the RNNE predicts. The latter is the analogue of bidding above the RNNE in high-bid-wins auctions.37 There are a number of issues in BD auctions that have yet to be explored. One important issue is the effect of BD auctions on longer-term relationships between buyers and their suppliers, as the latter are generally unhappy about participating in these auctions, claiming that they can harm longer-term relationships, with negative effects on longer-run costs and quality. Unfortunately, this is one issue that more than likely needs to be looked at in field data. However, what is known from experiments studying incomplete contracts (and other-regarding behavior in general) is that this may well be the case. But then the question is one of long-run versus short-run benefits. A second issue concerns how, and the extent to which, buyers account for quality characteristics, as it is rare for quality to be explicitly quantified before the auction takes place. This calls for continued investigations of alternative mechanisms accounting for quality differences in field data, and then investigating their properties in the lab. 1.8 Cash-Balance Effects and the Role of Outside Earnings On Bids In the typical auction experiment subjects bid in a series of auctions, with payoffs following each auction period. As a consequence bidders’ cash balances will vary over the course of the auction, which, for a variety of reasons, may impact bidding—for example, if subjects are risk averse or have earnings’ targets or earning aspirations that they bring to the experiment. Further, since these cash balances are endogenous, absent proper instruments they cannot simply be included as a right-hand-side variable in estimating bid functions since this will result in biased estimates for the variables of interest. Ham, Kagel, and Lehrer (HKL; 2005) investigate cash-balance effects in the context of a FPSB auction with affiliated private values (see Kagel, Harstad, and Levin 1987).38 HKL introduce exogenous variation in cash balances by simultaneously enrolling subjects in a lottery that has both positive and negative payoffs (with positive expected value). In this way they create their own instrumental variable to study the effects of cash balances on bids, in addition to a number of exogenous variables (e.g., ranking of bidders’ values) naturally produced as part of the experiment. They also varied the number of bidders in each auction with either 4 or 6 bidders competing in an experimental session in a between-groups design. Their results show a small, but statistically significant, negative cash-balance effect on bids; that is, the larger cash balances are, the lower subjects bid, other things equal. The quantitative effect of cash balances on the bid factor (the difference between bidders’ value and what they bid) is to increase it from $1.76 to $2.36 in auctions with 4 bidders and from $1.27 to $1.70 with 6 bidders (evaluated at the mean value for cash balances). KHL also estimate a time-trend variable (1/t, where t is the number of auction periods) to capture any learning/adjustments on the part of bidders. This shows that,

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other things equal, bid factors decrease over time. This is consistent with NS’s result (Section 1.1) that bids tend to increase with experience and feedback regarding auction outcomes. HKL estimate the impact of not including cash balances in the bid function. It biases the time-trend coefficient downward—so that there is less of an increase in bids over time. In addition, since in auctions with larger numbers of bidders, subjects have lower earnings and smaller increases in their cash balances (holding the support from which values are drawn constant), the impact of increased numbers of bidders is biased upward (as with larger N and a constant support, bidders earn smaller profits). HKL attribute the negative cash-balance effect to target income earnings and/or income aspirations on bidding. They conjecture that the mechanism underlying this effect is that subjects, who are recruited for the experiment with the promise of cash earnings, enter the auction with some target income earnings in mind and quickly recognize that they must win an auction to realize these earnings, which promotes higher bids at first. However, as cash balances accumulate, bidders come closer to their target earnings, which motivates them to take a chance on a bigger score by lowering their bids, even though this reduces their chances of winning. This effect is partly offset by the feedback regarding lost profit opportunities, which induces more aggressive bidding over time. This conjecture concerning the mechanism behind the cash-balance effect remains to be investigated directly. However, it does receive indirect support from at least one independent study.39 1.9 An Unresolved Methodological Issue In reviewing the auction literature, one does not have to look very far to identify two distinctly different ways of treating the data from different experimental sessions. One approach (one we have usually followed) is to enroll a relatively large number of subjects in each experimental session and to run several auctions simultaneously, randomly remixing subjects between groups in each auction. In reporting aggregate auction data (e.g., average revenue), we have pooled the data (after, perhaps, allowing for a learning period) and conducted either parametric or nonparametric statistical tests for treatment effects. In reporting more disaggregated data (e.g., estimating bid functions for treatment effects), the data are treated as a time-series-cross-sectional data set, with regression estimates based on (standard) random-effect models with a subject as the random effect, thereby accounting for obvious serial dependency in individual bid patterns (e.g., some subjects consistently bid well above the RNNE in FPSB auctions, others less so). A second approach is to take the subjects within a given experimental session and put them into subgroups, randomly rematching within the subgroups as opposed to over the entire sample population. For example, in a study of FPSB auctions with 4 bidders, with 16 subjects in each session, the investigator would form two 8-subject subgroups and randomly mix between them (as opposed to mixing over all 16 subjects in the session). The motivation for this is to obtain 2 “independent” sets of observations per session (the data for each 8-person subgroup) instead of only 1 independent group (the data for the 16 subjects in the session as a whole). The data analysis then proceeds on the basis of the aggregate behavior of these “independent” groups. The concern here is that in randomly rotating among all 16 bidders in the session, the repeated interactions between subjects would generate session-level effects that would dominate the data. This practice eschews the use of appropriate panel data techniques to correct for dependencies across

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and between subjects within a given experimental session, as well as to control for potential session-level effects. There are several important and unresolved issues in choosing between these two procedures. In both cases experimenters are trying to squeeze as much data as they can from a limited subject-payment budget, as well as a limited amount of time and energy available to investigate any given question. With the reader fully aware of our own biases on this matter, we note the following: First, advocates of repeated matching of the same smaller subset of subjects (1) often implicitly deceive subjects as they commonly do not report the rotation rule employed to subjects, and (2) if subjects are as sensitive to repeated matching effects as proponents of this technique assume, it seems plausible that repeated play within a small subset might generate super-game effects that will contaminate the data (whereas the models employed commonly assume one-shot games). Second, and more importantly, there have been a few experiments that have devoted time and effort to determine the severity of possible session-level effects from random rematching for the group as a whole. More often than not these studies find no differences with typical session sizes (e.g., Cooper et al. (1993; footnote 13, p. 1308) and Duffy and Ochs (2009). Also see Walker, Smith, and Cox (1987) and Brosig and Reiss (2007), who find no differences when comparing bids in auctions with all human bidders versus humans bidding against computers who follow the RNNE bidding strategy. More generally we think experimenters should treat this “independence” issue as an empirical one rather than a doctrinal one based on prior beliefs. In this respect, experimenters need to be sensitive to potential session-level effects and to employ appropriate econometric techniques (e.g., Fréchette 2012) as well as the old interocular eyeball technique in looking for, and adjusting for, possible session-level effects.

II SINGLE-UNIT COMMON VALUE AUCTIONS In common value auctions (CVA), the value of the item is the same to all bidders. What makes CVAs interesting is that although bidders don’t know the true common value, they receive signals (estimates) that are correlated (affiliated) with that value. Mineral-rights auctions (e.g., outer continental shelf—OCS—oil-lease auctions), are usually modeled as a CVA. There is a common value element to most auctions. Bidders for a painting may purchase it for their own pleasure, a private-value element, but also for investment and eventual resale, the common value element. Experimental research on CVAs has focused on the winner’s curse. Although all bidders obtain unbiased estimates of the item’s value, they typically win in cases where they have (one of) the highest signal value(s). Unless this adverse selection problem is accounted for, it will result in winning bids that are systematically too high, earning below-normal or negative profits—a disequilibrium phenomenon. Oil companies claim they fell prey to the winner’s curse in early OCS lease sales, with similar claims made in a variety of other settings (e.g., free-agency markets for professional athletes and corporate takeovers). Economists are naturally skeptical of such claims because they involve out-of-equilibrium play. Experiments reviewed in Kagel’s (1995) survey clearly showed the presence of a winner’s curse for inexperienced bidders under a variety of circumstances and with different experimental subjects: average undergraduate or MBA students (Bazerman and Samuelson 1983; Kagel and Levin 1986), extremely bright (Cal Tech) undergraduates (Lind and Plott 1991), experienced professionals in a

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laboratory setting (Dyer et al. 1989), and inexperienced bidders in auctions where it is common knowledge that one bidder knows, with certainty, the value of the item. Papers reviewed there also dealt with several alternative explanations for the winner’s curse— limited liability for losses (Hansen and Lott 1991; Kagel and Levin 1991; Lind and Plott 1991) and joy of winning (Holt and Sherman 1994). We pick up the story here with experiments investigating the ability of English auctions to raise revenue compared to FPSB auctions and auctions with experienced bidders where it is common knowledge that one bidder knows the value of the item. We look at behavior in “almost” CV auctions, where one bidder values the item more than others (with this being common knowledge), and bidding in auctions with both private and common value elements for all bidders. New results for the closely related “takeover” game are reported with the focus on sorting out between different explanations for the winner’s curse (WC). We report on the impact of demographic and ability variables on the likelihood of falling prey to the WC and what the lab results may or may not tell us with respect to behavior in field settings. The auctions reported on here, unless otherwise noted, use the following experimental design: The common value, x0 is the same for all bidders and is chosen randomly from a uniform distribution with support [ν, ν]. Each bidder i receives a private information signal, xi , about the unknown value of the item based on an iid uniform distribution with support [x0 − ε, x0 + ε]. 2.1 English Auctions Levin, Kagel, and Richard (LKR; 1996) implement an irrevocable-exit, ascending-price (English clock) auction. Prices start at ν, the lowest-possible value for x0 , and increase continuously. Bidders are counted as actively bidding until they drop out of the auction and are not permitted to reenter after that.40 The last bidder earns a profit equal to x0 less the price at which the last bidder dropped out. Bidders observe the prices at which their rivals drop out of the bidding. The irrevocable-exit procedure, in conjunction with the public posting of dropout prices, ensures that in equilibrium, bidders can infer their rivals’ signal values from the dropout prices. The analysis focuses on signals in the interval ν + ε ≤ x0 ≤ ν − ε. In a symmetric RNNE, the bidder who holds the lowest signal value (x L ) drops out of the auction once the price reaches x L .41 This dropout price reveals x L to the remaining bidders. Given the uniform distribution of signal values around x0 and the fact that in a symmetric equilibrium any remaining bidder j wins only when he or she holds the highest signal, each bidder j ought to use (x L + x j )/2 (a sufficient statistic for x0 ) as their dropout price in the symmetric RNNE. Dropout prices other than x L contain no additional information and should be ignored. Expected profits in the English auction are reduced by about 50% compared to a FPSB auction when more than two bidders are competing, so that the English auction is predicted to raise significantly more revenue compared to a FPSB auction. Earlier experimental results from FPSB auctions with x L publicly announced (Kagel and Levin (KL) 1986) showed that when bidders suffered from a WC, announcing x L lowered revenue (contrary to the theory’s prediction) as bidders with higher signal values recognized that they were overestimating the common value. However, once bidders had adjusted to the WC and were making reasonable profits relative to the RNNE benchmark, revealing x L increased revenue via the linkage principle, as the theory predicted. The key difference between LKR’s English clock auctions and these earlier FPSB auctions is that information dissemination is endogenous in the clock auctions

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rather than exogenous, when x L is publicly announced. As such, higher-signal holders must be able to recognize and process the relevant information, and low-signal holders must recognize the futility of remaining active once the price exceeds their signal value in order for the clock to increase revenue. Table 9.2 shows averages of predicted and actual changes in revenue between English and FPSB auctions for inexperienced bidders, with the results classified by the number of bidders.42 Average revenue is predicted to be higher in the English auctions in all cases for the set of signal values actually drawn, with significantly higher average revenue predicted for n = 4 for all values of ε and for n = 7 with ε = $12.43 However, for these inexperienced bidders, with the exception of n = 4 and ε = $24, actual revenue is lower in the English auctions, with significantly lower average revenue for n = 4 and 7 with ε = $6 ( p < 0.05) and for n = 7 and ε = $12 ( p < 0.10). These perverse revenue effects in terms of Nash equilibrium bidding theory are associated with negative average profits in both the FPSB and English auctions (see Table 9.2). The negative average profits indicate that inexperienced bidders suffered from a WC in both FPSB and English auctions, but that the curse was relatively stronger in the FPSB auctions. These results serve to generalize those reported for FPSB auctions with x L publicly announced (Kagel and Levin 1986): For bidders who suffer from a winner’s curse in FPSB auctions, release of public information reduces seller revenue rather than increasing it as the theory predicts. For more experienced bidders, English auctions raised average revenue with n = 4, with a statistically significant increase for ε = $18 (see Table 9.3). However, for n = 7, there was essentially no difference in revenue between the FPSB and English auctions. The significant increase in average revenue in English auctions with n = 4 was associated with the elimination of the worst effects of the WC in the FPSB auctions, as bidders earned a substantial share (more than 50%) of predicted profit. In contrast, with n = 7, bidders earned a relatively low share (21%) of predicted profits in the FPSB auctions, indicating substantially stronger residual traces of a WC, highlighting the importance of largely eliminating the WC in order for English auctions to raise revenue as the theory predicts. LKR develop an econometric model to characterize how bidders process information in the English auctions. As noted, the Nash bidding model predicts that bidders with higher signal values will average their own signal value with the first dropout price observed, ignoring all intermediate dropout prices. What they found, however, is that bidders placed weight on their own signal and the immediate past dropout price, ostensibly ignoring x L and any earlier dropout prices. Further, as more bidders dropped out, subjects placed less and less weight on their own signal and more weight on the last dropout price. This pattern, although inconsistent with the Nash model, is consistent with bidders acting “as if” they were averaging their own signal with the signal values underlying the dropout prices of all earlier bidders. LKR attribute the adoption of this signal-averaging rule to the fact that (1) it is easy and quite natural to use and (2) it yields results quite similar to the Nash rule without requiring that bidders explicitly recognize the adverse selection effect of winning the auction and/or knowing anything about sufficient statistics. One unanswered question raised by this analysis is if the signal-averaging rule would still be used with distribution functions, where it leads to markedly different outcomes from the Nash equilibrium. Would it still be used in this case as bidders would have more opportunity to recognize and respond to the profit opportunities inherent in abandoning the signal-averaging rule.

−1.32 (0.79) 1.20 (1.93)

2.76∗∗ (0.92)

8.10∗∗ (2.32)

0.54 (1.25)

1.09 (3.29)

$12

$24 [25]

[41]

[29]

9.83 (1.25)

5.01 (0.60)

2.76 (0.38)

0.11 (2.64)

−0.78 (0.95)

0.58 (0.50)

[13]

[45]

[28]

1.73 (2.14)

2.25 (0.69)

1.23 (0.30)

Theoretical

English

ND

−1.95 (1.19)

−1.98∗ (0.87)

Actual

ND

1.08 (0.65)

0.10 (0.34)

Theoretical

Average Change in Revenue: English Less First Price (Standard Error)

Notes: All values reported in dollars. + The null hypothesis that the value is greater than or equal to zero can be rejected at the 10% significance level. ∗ The null hypothesis that the value is greater than or equal to zero can be rejected at the 5% significance level. ∗∗ The null hypothesis that the value is greater than or equal to zero can be rejected at the 1% significance level. ND: No data Source: Levin, Kagel, and Richard (1996).

a

−2.13 (0.52)

1.54∗∗ (0.49)

−1.54∗ (0.72)

$6

Theoretical

Actual

Average Profit (Standard Error) First Price Actual

Theoretical

Actual

ε

Average Change in Revenue: English Less First Price (Standard Error)a

n=4

n=7

−3.75 (0.89)

−3.85 (0.71)

Actual

[30] ND

[18] 2.76 (0.53)

0.99 (0.19)

Theoretical

−1.80 (0.77)

−1.87 (0.51)

Actual

Average Profit (Standard Error) First Price

TABLE 9.2: Inexperienced bidders: actual versus theoretical revenue changes and profit levels in English versus first-price auctions.

[43] ND

[18] 1.68 (0.40)

0.89 (0.29)

Theoretical

English

3.96 (0.73)

2.98 (2.30)

1.20 (3.10)

∗∗

Theoretical

2.21 (0.95)

∗

Actual

Theoretical

6.77 (0.48) [163] 8.45 11.27 (1.28) (1.34) [31]

3.37 (0.50)

Actual

First-Price Theoretical

English

2.82 (0.53) [107] 7.25 8.29 (2.76) (1.93) [33]

1.16 (0.88)

Actual

Average Profit (Standard Error)

−0.25 (0.86)

Actual

ND

2.85 (0.61)

∗∗

Theoretical

Average Change in Revenue: English Less First Price (Standard Error)

0.76 (0.65)

Actual

ND

3.86 (0.50) [75]

Theoretical

1.01 (0.56)

Actual

Average Profit (Standard Error) First-Price

n=7

Notes: a All values reported in dollars. Super-experienced bidders had participated in at least two previous first-price common value auction sessions. ∗ The null hypothesis that the value is greater than or equal to zero can be rejected at the 5% significance level. ∗∗ The null hypothesis that the value is greater than or equal to zero can be rejected at the 1% significance level. ND: No data Source: Levin, Kagel, and Richard (1996).

$30

$18

ε

Average Change in Revenue: English Less First Price (Standard Error)a

n=4

TABLE 9.3: Super-experienced bidders: actual versus theoretical revenue changes and profit levels in English versus first-price auctions.

ND

1.01 (0.37) [96]

Theoretical

English

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TABLE 9.4: Change in seller’s revenue: auction with insider versus no insider (super-experienced bidders). n=4 Change in Revenue: Insider Less No Insider (t-stat) ε = $18 ε =$30

1.759 (2.057)∗ 2.734 (1.097)

n=7

Mean Profits (σ 2 ) Insiders

No Insiders

2.063 (8.561) 6.148 (24.334)

3.822 (49.972) 8.876 (59.371)

Change in Revenue: Insider Less no Insider (t-stat)

0.739 (1.573)+ 0.919 (0.425)

Mean Profits (σ 2 ) Insiders

No Insiders

1.492 (6.770) 4.517 (17.978)

2.231 (19.221) 5.436 (15.839)

Notes: ∗ Significantly different from 0 at p < 0.05, one-tailed test. + Significantly different from 0 at p < 0.10, one-tailed test. Source: Kagel and Levin (1999).

2.2 Auctions with Insider Information The standard common value auction (CVA) model assumes that all bidders are ex ante symmetric with respect to the quality of their signals (estimates) regarding the common value. It is quite natural to ask how robust the equilibrium is to the insertion of one bidder, an insider, who is better informed than the other bidders, outsiders. The easiest place to start this analysis is to assume that it is commonly known that there is a single insider with a better, more precise, estimate of the true value (at the extreme, an insider who knows the true value). Evaluating auction performance with an insider compared to the symmetric baseline depends quite critically on the baseline chosen. Wilson (1967) employed a symmetric baseline in which all bidders have only public information, so the seller extracts the entire surplus in the resulting mixed-strategy equilibrium (also see Hausch, (1987) and Hendricks, Porter, and Wilson (1994) for similar models). Introducing an insider into this environment reduces the seller’s revenue, as the insider can, and does, bid below the true value, earning positive profits. Since ex post efficiency is not an issue in a pure common value model, the insider’s gains must be the seller’s loss. We are unaware of any experiments that have investigated these predictions of the Wilson-type model. In contrast Kagel and Levin (KL; 1999) used the symmetric bidding model characterized in Section 2.1 as their baseline. Their “insider” treatment consisted of a single bidder who knows the true value with certainty, with all other bidders aware of this fact. “Outsiders” continued to draw signal values as in the symmetric bidding model. They did this to see if the presence of an insider who knows the true value would help bidders recognize the adverse selection effect conditional on winning, thereby mitigating—or possibly even eliminating—the WC. Although this hypothesis failed (inexperienced outsiders suffered from as strong a WC as inexperienced bidders with symmetric information), the experiment led to a very surprising and significant discovery: With more-experienced subjects who had learned to overcome the worst effects of the WC, earning substantial positive profits in FPSB auctions with symmetric information, the introduction of an insider actually increased seller’s revenues, as opposed to the decrease predicted in a Wilson-type model. Table 9.4 reports these results.

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This surprising outcome might have led some skeptics to dismiss this new finding, arguing that in laboratory experiments anything can happen. However, there is a critical difference between the experimental setup and a Wilson-type model. Unlike in Wilson-type models, in KL’s symmetric information benchmark model, all bidders have private information, so that in equilibrium the insider bids closer to the true value than in the Wilson model (because the “outsiders” have some private information). As a result, the introduction of a perfectly informed insider eliminates those symmetric information auctions where the winning bidder makes very large profits. (Evidence for this can be seen in the much smaller variance in average profits between asymmetricversus the symmetric information auctions reported in Table 9.3.) Further, unlike the early Wilson-type models, both insiders and outsiders earn positive average profits in equilibrium. What the two types of models do have in common is that conditional on winning, insiders make much larger average profits compared to outsiders because they have superior information.44 KL (1999) argue that many “real-world” cases are more realistically modeled, with outsiders having some proprietary information and not just public information. In these circumstances, it may well be the case that the introduction of a single well-informed insider increases average sellers’ revenue and that both insiders and outsiders earn economic rents. This potential for an insider to raise average revenue in a CVA had not been recognized in the literature prior to this. 2.3 Common Value Auctions with an Advantaged Bidder The standard CVA model assumes that all bidders have exactly the same value for the item. But how robust, theoretically and in practice, are the properties and performance of auctions to slight departures from this assumption? In many common value auctions it is common knowledge that one (or more) bidder(s) (advantaged bidders) get an extra payoff relative to the other (regular) bidders; for example, in the FCC regional airwaverights auctions, Pacific Telephone was widely believed to place a higher value on the West Coast regional area than their potential rivals because of their familiarity with the region and their existing customer base (Klemperer 1998). Economic theory suggests that with two bidders and a SPSB or English auction, even the tiniest private value advantage can have an “explosive” effect on auction outcomes, with the advantaged bidder always winning and earning very high profits (sharply reduced revenue; Bikchandani 1988; Klemperer 1998). However, the question of whether or not these predictions will emerge depends critically on bidder behavior. It is here where experiments can help sort out when, where, and why we ought to be concerned about such explosive effects. Avery and Kagel (AK; 1997) investigated the explosive effect of a small private private value advantage in a SPSB “wallet-game” auction. Two bidders bid in a SPSB auction for the value of a wallet with two cells, where each of them privately observes the content of one of the cells. Let x1 and x2 represent the privately observed signals by the first and second bidders, respectively. The value of winning the wallet for these bidders is V1 = x1 + x2 = V2 . Bidding twice their observed signal, b(xi ) = 2xi , i = 1, 2, is both a unique symmetric equilibrium as well as an ex post equilibrium in which bidders have no regret. Further, it is distribution free and independent of risk preferences. With a private value advantage, the valuation of the advantaged bidder (say, bidder 1) becomes: V1 = x1 + x2 +  (or V1 = x1 + x2 + x1 ), where  > 0 is presumed small. Essentially what the private-value advantage does is to destroy the symmetric

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equilibrium of the SPSB auction. In the resulting asymmetric equilibrium, the private value advantage has a “snowball” effect, resulting in the advantaged bidder winning all the time, bidding too high for the disadvantaged bidder to profitably unseat him or her. This does not happen in a FPSB auction but does in a SPSB auction, as the high bidder does not have to pay what he or she bids. However, in the experiment, where the advantaged bidder valued the item at $1 more than the disadvantaged bidder, the effect of the private value advantage was proportional rather than explosive as, controlling for signal values, the difference in bids was closer to the private value advantage of $1 than to the $3 difference predicted under the explosive effect. In effect, both advantaged and disadvantaged bidders were bidding closer to the naïve expected value of the item conditional on their signal value, with the advantaged bidder simply adding their private value advantage to their estimate. AK explore a number of alternative explanations for this outcome. None fit as well as the naïve behavioral model in which advantaged bidders simply add their private value advantage to their estimate of the common value. Rose and Levin (2008; RL) investigate the effect of a private value advantage in the two-person wallet game, this time using an English clock auction. The key motivation for this experiment is that in virtually all experimental work behavior is much closer to equilibrium predictions in English clock auctions compared to sealed-bid auctions (Kagel, Harstad, and Levin 1987; Levin, Kagel, and Richard 1999; Kagel and Levin 1999). As such there is a clear need to explore the model in an English auction before concluding that small asymmetries do not matter very much, particularly since English auctions are far more common than SPSB auctions. RL do not find any evidence of the explosive effect either, with players clearly suffering from the winner’s curse in both the symmetric and asymmetric auctions, as evidenced by the frequency with which they lost money. When tested against the data, the Nash equilibrium model and the expected value hypothesis (naïve expectations) are both rejected, although the expected value hypothesis provides a better fit than the Nash model.45 Summary. The results of all reported CVA experiments with a private value advantage show that contrary to what the theory predicts, a private value advantage leads to proportionate responses as opposed to the explosive effect predicted. The apparent reason for these failures is that bidders do not fully appreciate the adverse selection effect conditional on winning, which is exacerbated for regular bidders when facing an advantaged rival. As such, the behavioral mechanism underlying the explosive effect is not present, and there are no forces at work to replace it. This leaves us quite skeptical of finding similar effects outside the lab under the conditions the theory specifies. Indeed, it would seem to require very sophisticated bidders for the explosive effect to be realized under these conditions. As such, we would expect that bidders outside the laboratory would employ alternative strategies available to them in the less structured environment in which they operate to press their private value advantage. PacTel appears to have done something like this in the FCC major trading area (MTA) sale of broadband personal communication licenses for Los Angeles and San Francisco. PacTel, which held a substantial private value advantage, publicly announced their intentions to top their opponents’ bids, while obviously having the resources and a sufficiently large private value advantage to make such an announcement credible (see Cramton 1997), a strategy that lies outside the formal theory. As a side note, PacTel got the licenses in question, but they were only partially successful in obtaining rock-bottom prices, as there was rivalrous bidding based on the personalities of the leading bidders, another element left out of the formal

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theory. More generally, Cramton notes, there is likely to be some incentive in CVAs with a private value advantage for predatory bidding on the part of rivals, thereby offsetting the revenue-reducing forces implied by the explosive effect. 2.4 New Results in the Takeover Game: Theory and Experiments The systematic overbidding resulting in a WC for inexperienced bidders has attracted the attention of theorists in efforts to explain the WC within a generalized Nash bidding model that permits a more relaxed belief system. Eyster and Rabin (ER; 2005) generalize the Nash model by introducing the notion of a “cursed equilibrium,” in which bidders correctly predict, and best respond to, the distribution of others’ bids but do not correctly perceive how these other bids depend on other bidders’ signals. This model rationalizes deviations from the standard Nash equilibrium, depending on the degree of “cursedness” bidders suffer from. Crawford and Iriberri (CI; 2007) rationalize the WC within the context of a level-k reasoning model. Roughly, they allow different levels of “sophistication,” where they define a level-0 player as a bidder who picks randomly from the allowable set of actions, with more sophisticated players best responding to all other players being one level less sophisticated than they are (so level 1 best responds to level 0, and level 2 best responds to level 1). The remarkable thing about this approach is that (1) a combination of level 1 and level 2 players explains the high frequency of WC for inexperienced bidders in FPSB auctions and (2) the estimated frequencies of the two player types closely matches the frequencies reported in a variety of other, unrelated, experiments (having (1) without (2) would simply be an exercise in data fitting).46 Both the ER and CI models apply to CVAs and the closely related “take-over” game. Nash equilibrium bidding in CVAs requires complicated calculations of best responding to other bidders actions, involving both beliefs about others rationality and strategic uncertainty. To circumvent these complications, Charness and Levin (CL; 2009) employ a modified version of the takeover game, turning it into an individual decision-making problem where avoiding the WC does not depend on beliefs about other bidders’ actions. In the take-over game (first studied in Samuelson and Bazerman, 1985), there are two players, a buyer (the acquiring firm) and a seller (the target firm). The buyer knows that the target’s value, VS , is a random variable uniformly distributed in the interval [$0, $100]. The value of the target firm to the buyer, VB , is VB = 1.5VS . The buyers do not know VS when placing their bids but know that the seller does and that the seller employs the dominant strategy of accepting only offers that are greater than or equal to VS . In spite of the simplicity of this game, which abstracts from many of the complications embodied in a multiplayer auction context, subjects still suffer from not recognizing the adverse selection effect conditional on winning and succumb to the WC, bidding somewhere between the unconditional expected value to the seller of 50 and the unconditional expected value to the acquirer of 75 (as opposed to the optimal bid of 0; see Kagel (1995) and Kagel and Levin (2002) for summaries of results from these experiments). CL transform the game into an individual-choice task where subjects make a bid and then choose one of 100 “cards” numbered {0, 1, 2, . . . , 99}, that are displayed facedown on the computer screen. The same rules apply as in the takeover game in that if the card chosen is less than or equal to the bid, players receive 150% of the current value of the card less their bid and zero otherwise. However, there are no other human agents whose behavior bidders need to establish beliefs for, either in the sense of ER or CI.47

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0.60 Less detail More detail

Frequency

0.45

0.30

0.15

0.00 0-9

10-29

30-49

50-69 70-89 Bid range

90-100

100+

Figure 9.5: Bid frequencies in two-value takeover game.

CL find average bids to be 38.9, which is lower than the 50–75 average typically reported when the game is framed in terms of sellers accepting or rejecting bids. Further, there is a higher proportion of very low bids in the 0–9 range (around 25%) than typically reported. To further simplify choices, CL modify the game even further, employing just two possible card values, 0 or 99. This treatment circumvents the need to use Baye’s law to construct posterior beliefs, as well as the need to recognize the implications of the firm’s values being drawn from a uniform distribution. Now, without any calculations, it should be clear that 0 dominates any bid except for 99. Further, in choosing between 0 and 99, the choice of 99 involves a rather unattractive gamble between a positive profit of 49.5 or a negative profit of 99, with both outcomes equally likely, for an expected profit of negative 24.25. Figure 9.5 reports the results from this last treatment under two sets of instructions, with one providing more detail than the other. While there are relatively few bids other than 0 and 99, 47% of all bids are 99. Since the latter may reflect a need for some “action” as opposed to always bidding zero, CL further modify the game so that the card values are either 20 or 119. Now, bidding 20 yields positive expected profit. This results in an even further reduction in the frequency of nonoptimal bids to 30%.48 Finally, CL have subjects choose between lotteries whose payoffs are equivalent to the 0–99 and 20–119 treatments, which serve to rule out risk loving as a possible explanation for nonoptimal bids. CL note that taken literally, converting the takeover game to an individual-choice problem rules out both the ER and CI models as an explanation for the winner’s curse, since there are no other players whose actions must be taken into account. However, assuming that subjects still frame the situation as a two-player game, with the computer as the second player, results from the two-card treatments are inconsistent with both models because they predict all bids will be 0 (in the 0 or 99 treatment) or 20 (in the 20

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or 119 treatment). CL conclude that the fundamental problem underlying the winner’s curse is the failure to fully account for payoffs contingent on winning the auction. One possible limitation of CL’s results is that in transforming the problem into an individual-choice task, this still leaves open the possibility that models that incorporate best-response behavior but allow for inconsistent beliefs may explain the WC in auctions. To address this issue, Ivanov, Levin, and Niederle (2010) employ a SPSB CV auction called the maximal game, in which two players receive an iid signal, with the common value of the item equal to the highest signal drawn. The maximal game is dominant solvable in two iterations, so that overbidding (the WC) can be rationalized only by cursed (or k-level) beliefs—a bidder believes that others are using dominated strategies (in this case bidding below their signal values). They investigate this by (1) exogenously disallowing underbidding and (2) by having subjects bid against their own bid from previous auctions. Neither of these two treatments eliminates the WC. There is minimal tendency toward downward correction of bids in both treatments as well. These results, together with CL, strongly suggest that the WC in laboratory experiments represents a more fundamental departure from Nash equilibrium bidding than simple inconsistency of beliefs. Quantal response equilibrium, which relaxes the requirement for strict best responding, is at odds with the ILN data as well. 2.5 Additional Common Value Auction Results 2.5.1 SUPER EXPERIENCED BIDDERS Kagel and Richard (KR; 2001) investigate bidding for superexperienced bidders— subjects who had participated in at least 2, and up to 4, prior CVA sessions. These superexperienced bidders had learned to overcome the worst effects of the WC in FPSB auctions, rarely bidding above the expected value conditional on winning. However, they still earned less than 50% of the Nash profits (at a cost of between $2.50 to $3.50 per auction, conditional on winning). KR examine a number of elements that might be responsible for the continued shortfall relative to the RNNE benchmark. They first look at the bid function itself, which is quite complicated over the full support from which signals are drawn, if this is responsible for the shortfall in profits relative to the RNNE benchmark. They find that bidders use sensible piecewise linear bid functions rather than the more complicated Nash bid function. But simulations show that there exists a symmetric rule-of-thumb equilibria (RTE; in which bidders are restricted to using piecewise linear bid functions of the sort estimated) in which profits are equal to or greater than the RNNE benchmark. As such, bidders’ inability to account for the complexities of the Nash bid function cannot account for the marked reduction in their earnings. KR then show that subjects are not best responding to bids in excess of the RTE with losses relative to best responding averaging 20% and 44% in auctions with 4 and 7 bidders, respectively. Thus, very experienced bidders still suffer from a WC, albeit one that is much less pronounced and more subtle than the negative average profits inexperienced bidders suffer from. KR suggest two primary reasons for these continuing losses relative to the RNNE and the RTE benchmarks. First, best responses are highly variable in small samples of the sort that bidders would have seen, sometimes pointing in the wrong direction (bid higher) compared to large-sample estimates and sometimes calling for overly passive bidding (bid below x − ε). This makes best responding far more problematic than the large-sample estimates suggest and could lead bidders to simply ignore any feedback

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once consistently positive profit were earned. Second, large-sample best responses require winning half as many auctions as were actually won. This involves a rather dramatic change in bidding, assuming that bidders are able to identify this fact, so that here, too, subjects may be reluctant to deviate from a rule of thumb that has proved capable of generating acceptable profit levels (compared to their inexperienced selves) in such a high variance environment. 2.5.2 AUCTIONS WITH BOTH COMMON AND PRIVATE VALUE ELEMENTS One of the simplifications in standard auction theory is that bidders are dealing with either a pure common value or a pure private value environment. However, most realworld auctions have both private and common value elements. For example, bidders for oil leases have an estimate of the common value but may have an idiosyncratic cost of extracting the oil and delivering it for refining, resulting in both a common value and a private value estimate of the value of the lease. The theoretical difficulty with multiple signals is how to combine them into a single statistic that can be mapped into a bid. Goeree and Offerman (2003) develop one such model and investigate it experimentally (Goeree and Offerman (GO; 2002).49 GO employ a series of FPSB auctions, the main objective of which is to evaluate those factors their model predict will raise efficiency and revenue. These consist of (1) reduced variance in the signals for the CV component, which ought to make the auction more efficient as it moves the environment closer to a pure private value auction, (2) increased numbers of bidders, which, in their model, reduces the weight bidders place on the CV component of their signal, thereby increasing efficiency, and (3) the release of public information that reduces the importance of the CV element, thereby increasing revenue (as in a pure CVA) and improving efficiency. In all treatments, both the “rational” bid function, in which bidders fully account for a potential WC, and a naive bid function, in which bidders fail to do so, predict the same winner as they are both functions of the same summary statistic, so there is no efficiency loss in their design due to a WC. GO report that the winner’s curse is alive and well in their experiment because bids lie in between the naïve and Nash benchmarks (see Figure 9.6) even for experienced bidders, and lie closer to the naïve benchmark the less important a bidder’s private value is relative to the common value.50 The WC serves primarily to raise revenue and reduce bidders’ profits, with realized efficiency roughly at the level predicted under the RNNE. The latter occurs because (1) almost all bidders suffer from a WC and (2) the degree of suffering is roughly the same across bidders, so that the private value element of a bidder’s signal serves to dictate who wins the auction. As predicted, efficiency increases with decreasing variance in the signals for the CV component and with increases in the number of bidders. Ignoring their low-variance treatment, with its minimal scope for a WC, public information regarding the CV component increases bidders’ profits in 4 out of 5 treatments, consistent with the comparative static prediction of the naïve bidding model and the results reported in KL (1986). 2.5.3 SELECTION BIAS, DEMOGRAPHIC, AND ABILITY EFFECTS The transition from inexperienced bidders suffering persistent losses to experienced bidders earning respectable profits in CVA experiments is characterized by large numbers of bidders going bankrupt, with these bankrupt bidders much less likely

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325

275

225 Bid

594

175

125

75 75

100

125

150

175

200

Surplus Figure 9.6: Bids in auctions with both common value and private value components.

to return as experienced subjects. Further, the WC involves a judgmental error—the failure to account for the adverse selection effect conditional on winning—so that it joins a growing literature suggesting that limited cognitive abilities might help to explain many of the observed deviations from full rationality reported in economic experiments. Casari, Ham, and Kagel (CHK; 2007) conduct an experiment designed to better understand the process whereby experienced bidders learn to avoid the WC, as well as the impact of cognitive ability and demographic effects on learning to overcome the WC. Cognitive ability is measured by Scholastic Aptitude and American College Test (SAT/ACT) scores collected from university records. University records also provided information regarding a subject’s college major, grade point average (GPA), and gender (all collected with subjects’ permission). Subjects participated in two sessions approximately 1 week apart. To better understand the learning process, starting cash balances were randomly varied across bidders, with additional random shocks generated via a lottery with positive expected value. Further, some sessions followed standard experimental procedures, inviting all subjects back for additional sessions without any special inducements to return, while others recruited subjects who were committed to returning and were provided strong incentives to do so in the form of a relatively large show-up fee (to be paid at the end of session 2), with half of session 1’s earnings withheld until completion of session 2. In this way CHK hoped to distinguish between learning via market-selection effects (less able bidders going bankrupt, exiting the market, and not returning for subsequent experimental sessions) versus individual bidders learning to avoid the WC. CHK report a number of results: First, not surprisingly, ability as measured by SAT/ACT scores matters in terms of avoiding the WC. However, the nature of these

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ability effects is different from what one might expect as (1) composite SAT/ACT scores were consistently more significant than either math or verbal scores alone and (2) the biggest and most consistent impact was that subjects with below-median scores were more susceptible to the WC, as opposed to those with very high scores doing exceptionally well. Second, there were clear demographic effects as inexperienced women were much more susceptible to the WC than men, even after controlling for ability and college major, factors that are not typically controlled for in investigating gender effects in experiments.51 However, women learned faster than men, so that this difference disappeared with experienced bidders. Economics and business majors were much more susceptible to the WC than other majors, and continued to earn lower profits even as experienced bidders controlling for SAT/ACT scores and gender. Third, controlling for selection effects, bidders are capable of substantial individual learning, even those subjects who start out being most susceptible to the WC. However, more-able bidders were more likely to return as experienced subjects, with this factor dominating learning between weeks 1 and 2 for those sessions that did not employ special inducements to get subjects to return. As such, previous studies that have not controlled for this selection effect are likely to have substantially overestimated the amount of individual subject learning that occurs when moving from inexperienced to experienced bidders. CHK also find that standard econometric estimators for dealing with selection effects in field data do not identify them in their data, in spite of having a relatively large sample by experimental standards and well-identified econometric models. However, the different treatments built into the experimental design serve to identify, measure, and verify these effects. The latter is not surprising, since at least as far back as Fisher (1935), statisticians have understood that good experimental design helps in identifying causal effects. As to why economics and business majors were more susceptible to the winner’s curse, CHK suggest that this is more than likely a personality effect, with business and economics students by nature more aggressive in business-type transactions. An alternative hypothesis, that “a little knowledge is a dangerous thing,” is rejected on the grounds that subjects were drawn primarily from introductory economics classes, which do not cover issues like the WC. The gender effect is much more difficult to explain. Two known factors that immediately come to mind, that women tend to be more risk averse than men and that men tend to be overrepresented in the upper tail of mathematical reasoning, fail as (1) risk aversion cannot explain succumbing to the WC since it involves earning negative expected profits and (2) the estimated bid functions show that mathematical ability does not play a critical role in succumbing to the WC (and was controlled for in the statistical analysis). CHK conjecture that the greater susceptibility of women to the WC may reflect a relative lack of experience with strategic interactions compared to men, perhaps as a result of women shying away from competition more than men (Niederle and Vesterlund 2007; see Chapter 8 as well). This relative lack of familiarity might induce more aggressive bidding as a consequence of the failure to fully think through its implications. Remark. CHK also compared their sample population to the university population from which their sample was drawn. The most interesting result here is that 20.2% of their sample were in the top 5% (of the national average) with respect to composite SAT/ACT scores (versus 4.9% for the university), with less than 8.9% scoring below the median (versus 20.9% for the university), indicating that much brighter students tend to enroll in economic experiments.

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2.6 Is the Winner’s Curse Confined to College Sophomores? One inevitable question raised by laboratory experiments is whether the behavior reported is confined to the typical population of convenience, undergraduate students, as opposed to “real people” in field settings. Kagel’s (1995) survey addressed this question in two ways: First, it reported a number of striking similarities between anomalous field data and the experimental outcomes that could be directly attributed to the WC.52 Second, results from a laboratory experiment comparing experienced bidders from the construction industry with student subjects showed that both suffered from a strong WC (Dyer, Kagel, and Levin 1989). Follow-up research suggested two key factors, which are not mutually exclusive, behind the executives’ performances in the lab and their apparent success in the field (Dyer and Kagel (DK; 1996): One is that the executives had learned a set of situation-specific rules of thumb that permit them to avoid the WC in the field but that could not be applied in the laboratory, such as their specialized experience with a given branch of the construction industry or familiarity with the architect responsible for supervising the work. Second, the bidding environment created in the experiment, which is based on theoretical work, is not fully representative of the environment encountered in the construction industry; for example, repeated-play elements present in the field typically permit bidders to pull winning bids that are clearly too low relative to the expected cost of the project and to do so without penalty. Harrison and List (HL; 2008) report results that appear to be at odds with the contactor results. In their experiment they compare bids by sports card dealers with nondealers in a laboratory-type setting under two structures: (1) the symmetric information structure employed in Kagel and Levin (1986; all bidders’ signals are randomly drawn from the interval [x0 − ε, x0 + ε]) and (2) the asymmetric information structure employed in Kagel and Levin (1999, where one bidder knows the true value, xo , with certainty while all other bidders get a signal drawn from the interval [x0 − ε, x0 + ε]. In both treatments subjects bid in a single auction after having participated in at least 10 practice auctions to familiarize subjects with the rules of the auction. Treatments included two different values of ε ($6 and $12) and two different levels of competition— auctions with 4 and 7 bidders.53 Their results show that with symmetric information, dealers rarely suffer from a WC, while nondealers do, with these differences statistically significant at conventional levels. Further, there are significant differences in the estimated bid function between dealers and nondealers, with much of the difference resulting from the sharper discounting of bids relative to value with ε = $6 for dealers.54 In contrast, in the asymmetric information laboratory treatment, HL are unable to reject a null hypothesis that dealers, in their role as outsiders, bid differently from nondealers, with dealers suffering from a nonnegligible frequency of the WC (in 25% to 30% of all auctions). HL interpret their results as follows: The absence of a WC with symmetric information is consistent with the notion that dealers have experience in comparable settings. Further, since this experience is generated in the field and not in the lab, it supports the notion that “context-specific experience does appear to carry over to comparable settings, at least with these types of auctions” (Harrison and List 2008, 839). However, once dealers are taken out of their comfort zone, bidding as outsiders in the asymmetric information auctions, a role HL argue dealers rarely occupy in field settings, they look very much like the student subjects. In our view, at a minimum HL’s results provide additional evidence for very limited learning generalizability: dealers having adapted to adverse selection effects in field settings with symmetric information do not recognize

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the heightened adverse selection effect when an insider is present, succumbing to the WC. This is consistent with the psychology literature on learning generalizability, which indicates that learning transfer, unless specifically taught for, does not generalize easily across different domains, and the more different the domains, the harder it is to obtain positive learning transfer.55 Given the limited learning generalizability identified in HL’s data, in conjunction with the psychology literature on the subject and DKL’s results with construction contractors, we offer the following alternative explanation for the apparent transfer of learning in the symmetric information environment: it may well rest on a heuristic that travels well, as HL claim, but one that is not related to the WC and that adventitiously protects dealers from the WC in the symmetric information case. Namely, dealers are in the habit of buying low and selling high; for example, List and Lucking-Reiley (2000) show that dealers bid just under $50 for cards with a retail value of $70 in a Vickrey auction (also see Garret, Walker, and Wooders 2012). Applying such a large discount relative to their signal value could very well protect dealers from a winner’s curse. In contrast nondealers, who buy for their own use, would not be in the habit of applying such a large discount. We are not sure how to sort out their explanation from ours. However, we would note that, to the extent dealers have experience with buying and selling objects with a significant CV component, they do so in established markets with established prices for sports cards and sports memorabilia, leaving little scope for any kind of an adverse selection effect. Remark. HL also report a treatment in which subjects bid to purchase an unopened package of Leaf sports cards, packages containing 10 cards of unknown value, and an established retail price of between $9 and $10. They argue that this represents a CVA, with which we agree. However, it is not one in which there is any scope for a WC, since the cards have an established market value; that is, there is no scope for an adverse selection effect based on different estimates of value that anyone but a very poorly informed buyer might have. As such, this exercise is comparable to auctioning off a $10 bill. Plots of bid distributions bear this out because there is not a single bid above $10 for dealers and only a handful of bids above $10 for nondealers. HL also make a number of broader and related claims, at least one of which deserves further discussion. They claim that the absence of a WC among dealers in both the Leaf trading card treatment and in the more abstract laboratory treatment with symmetric information is “consistent with the conclusion that dealers in the field do not fall prey to the winner’s curse providing tentative support for the hypothesis that naturally occurring markets are not in disequilibrium because of the WC” (Harrison and List 2008, 823–24, italics in the original). Here, we would remind the reader that the term winner’s curse was initially coined by three petroleum geologists (Capen, Clapp, and Campbell 1971) reporting on results from early outer continental shelf (OCS) oil-lease auctions in an effort to explain low (or below normal) returns on these leases. This claim, as well as similar claims in other settings, is what originally motivated experimental work investigating the WC.56 The fact that subsequent laboratory experiments showed that the WC is alive and well, persistent, and robust, indicate that it is likely to exist at least in the start-up phase of auction markets with a strong CV element. Finally, let us assume that HL are correct that in relatively settled markets with very experienced bidders survivors no longer fall prey to the WC. To us this is similar to arguing that in a population ravaged by an infectious disease, the disease no longer exists since the survivors have developed immunity to it. This does not, however, imply that should a

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significant variation of the disease—or a new disease—strike the surviving population, they will be able to do any better than the original population.

III MULTIUNIT-DEMAND AUCTIONS Theoretical and experimental research up to 1995 focused almost entirely on auctions where each bidder demands a single unit of a homogenous commodity. Not much changes in the theory if there are multiple units for sale as long as individual bidders continue to demand a single unit. However, in auctions where bidders demand multiple units, outcomes can change rather dramatically. The FCC airwave-right (spectrum) auctions in the 1990s provided the main incentive to better understand auctions where bidders demand multiple units, raising a host of new issues, many of which are of public policy importance. (The extensive use of Internet auctions also has played a major role in stimulating auction research; see Section 4.3.) Where and how can one design efficient multiunit demand auctions? Are efficient multiunit demand auctions very different from optimal (revenue-maximizing) auctions? Multiunit demand auctions also call attention to a much richer strategic environment, where bidders may exercise demand reduction, bidding “passively” on some units in order to obtain other units at low prices. They also call attention to the difficult case of complements, with strong synergies generated as a consequence of winning multiple units, and the potential role of package bidding to help achieve more efficient outcomes. In looking at multiunit demand auctions, we need to distinguish between smallscale, traditional laboratory experiments designed to investigate some of the new theoretical/behavioral issues identified in the literature as opposed to market-design issues. In the latter, the laboratory serves as a “wind tunnel” for comparing different mechanisms for specific public policy purposes. There are limited numbers of comparable market design experiments against which to evaluate results (and often not much emphasis on the behavioral mechanisms behind the results reported). We will review the more traditional small-scale experiments that focus on behavioral issues, with market design issues covered in Roth (Chapter 5). 3.1 Auctions with Homogeneous Goods—Uniform Price and Vickrey Auctions In multiple-unit, uniform-price (UP) auctions, items are allocated to the high bidders at a price equal to the highest rejected bid. With bidders demanding multiple units, if the goods are substitutes, bidders have an incentive to reduce demand in an effort to obtain more favorable prices on the items actually won (Ausubel and Cramton 1996; Engelbrecht-Wiggans and Kahn 1998). The argument for demand reduction is essentially the same as a monopsonist as the price they pay will increase when competing to buy additional units. Cramton (1997) argues that the first nationwide FCC spectrum auctions could be best modeled as UP auctions of this sort. Kagel and Levin (KL; 2001) experimentally investigate the sensitivity of bidders to these demand-reduction possibilities, comparing behavior under a uniform-price sealed-bid (UPSB) auction with an English clock auction in which bidders receive information regarding rivals’ drop-out prices as the auction progresses. They study behavior in the simplest possible setting while still preserving the essential strategic elements of more complicated auctions: a human subject with flat demand for two units of a homogeneous commodity competes against different numbers of rivals demanding

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a single unit of the commodity, with the role of single-unit buyers played by computers whose bids are equal to their private value (the dominant strategy). With IPV draws from a uniform distribution and supply of 2 units, the equilibrium prediction for the “large” (human) bidder is to bid his or her value on unit 1 and to bid sufficiently low on unit 2 so as to not affect the market price.57 This holds irrespective of the value of the item, the number of computer rivals, or whether a UPSB or English auction format is used. For the UPSB auctions, this requires bidding zero on the second unit, which is far from transparent. In contrast, the optimal bidding strategy in the clock auctions requires dropping out on the second unit at a price p ∈ [0, v2 ], where v2 is the dropout price of the second-highest computer rival. This has exactly the same consequences as dropping out at 0, but the feedback information provided by rivals dropping out, and the flexibility in the dropping rule, make the optimal bidding strategy substantially more transparent.58 Results from this experiment showed clear evidence of demand reduction in the UPSB auctions but with substantially more demand reduction in the English auctions: 30.8% of all unit 2 bids were pivotal (higher than v2 , thereby setting the market price) in the sealed-bid auctions compared to 11.4% in the clock auctions.59 However, there were even more striking differences between the two auction formats: (1) There was a much higher frequency of bidding above value on the first (and even the second) unit in the UPSB auctions (comparable to the results for SPSB auctions) and (2) there were relatively few bids at 0 in the UPSB auctions, required to ensure not being pivotal. Figures 9.7 and 9.8 illustrate these differences between the English auction and the UPSB auction with five computer rivals. KL show that the primary basis for the superior performance of the English clock auction over the UPSB version results from the feedback information regarding the computer’s drop-out prices. They did this in two ways. First, they conducted an English auction in which there was no feedback regarding dropout prices, with the auction ending when the last bidder dropped out. In this case the English auction was of no help to bidders, as demonstrated by massive bidding above value on both units, quite similar to what was found in the UPSB auctions. They also conducted a UPSB auction in which v2 was posted in a prominent place on bidders’ computer screens. Subjects were not told how to use the information, just what it was and that it had been suggested that the information might prove helpful in determining how to bid. This treatment went a long way to moving the UPSB outcomes closer to the English auction results as it (1) essentially eliminated the overbidding on unit 1 and (2) resulted in a level of demand reduction closer to the one reported for the English auctions. KL also compared outcomes from these uniform-price auctions to a dynamic Vickrey/Ausubel clock auction (Ausubel 2004). This version of the Vickrey auction with dropout information provided employs a “clinching” metaphor from sports leagues to characterize prices paid.60 It generates sincere (value) bidding in iterated deletion of dominated strategies and, under KL’s demand structure, raises more revenue than the uniform-price auctions. Results from the Ausubel auctions are shown in Figure 9.9 with five computer rivals, where outcomes are reasonably close to sincere bidding. Using bidders’ actual earnings relative to predicted earnings as a measure of how close bidders were to optimal outcomes, KL establish a clear ranking for the three auction institutions studied in terms of the frequency with which they were within 5% of maximum earnings: 13.6%, 46.5%, and 85.2% for the UPSB, uniform-price clock auction, and the Ausubel auction, respectively. KL conclude that, like the UP clock

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auction with feedback, the Ausubel auction benefits from the clock procedure with feedback to prevent overbidding. However, unlike the uniform-price clock auction, the Ausubel auction encourages nonstrategic bidding (full demand revelation), something that bidders are inclined to do even in the uniform-price auctions. Thus, the closerto-optimal performance in the Ausubel auction partly results from an institution that accommodates itself to bidders’ natural tendencies. Remark. KL’s UPSB auction included explicit advice against subjects bidding above their values, along with examples as to how this could lead to losses. The motivation for this was to speed up equilibrium outcomes on unit 1 bids, a “nuisance” factor in terms of KL’s primary interest in demand reduction on unit 2 bids. Referees criticized these procedures as biasing the SB auctions too strongly in favor of equilibrium outcomes, in response to which additional sessions were run dropping the advice. As anticipated, the

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primary impact was to reduce the frequency of unit 1 bids above value, with essentially no impact on the overall frequency of demand reduction. The point of this remark is that by the turn of the century, with experiments firmly entrenched in the economist’s tool kit and behavioral economics making its way onto the stage, referees and editors of a major journal were concerned with biasing procedures in favor of the theory. From our personal experience, this reflects a significant (and welcome) shift from earlier referees (and journal) biases in favor of experimental outcomes supporting a theory, with little regard, in some cases, to procedures that favored the theory. There have been a number of subsequent experiments using all human bidders investigating demand reduction in uniform-price auctions. Porter and Vragov (2006) investigate both a UPSB and clock auction, along with a sealed-bid Vickrey auction. Sessions consisted of 30 auctions, with randomly drawn valuations, supply of 2 units

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with 2 (randomly matched) bidders, each demanding 2 units, sometimes with different values and other times with the same values.61 Their results largely replicate those reported in KL. First, for the UPSB auctions, there is rather massive overbidding with respect to unit 1 bids and relatively large-scale demand reduction with respect to unit 2 bids (see Figure 9.10). For the clock auctions, unit 2 prices are close to their starting price and well below prices in the sealed-bid auctions, consistent with strong demand reduction. Their SB Vickrey auctions exhibited substantial bidding above value for both units (see Figure 9.11), consistent with the results reported for SPSB auctions. There have been a number of other experiments investigating these issues. largely replicating the main results reported so far: List and Lucking-Reiley (LLR; 2000) look at demand reduction in a field experiment with subjects bidding for sports cards,

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with subjects participating in a single auction. Since LLR do not know bidders’ value for the sports cards, they employ a parallel series of SB Vickrey auctions (in which sincere bidding is a dominant strategy) as the reference point against which to evaluate demand reduction in the UPSB auctions. Engelmann and Grimm (EG; 2009) conduct an experiment in which subjects participated in a series of auctions with limited repeat pairings, with 2 homogenous items for sale and 2 bidders with flat demand for both units. They look at demand reduction in both UP clock and UPSB auctions and compare outcomes with a dynamic Vickrey (Ausubel) auction and a static Vickrey auction.62 After factoring out occasional collusive efforts resulting from repeat parings, their primary results are well in line with those reported so far. They and others working on these issues note that contrary to the theory, the UPSB auction generates higher revenue but lower efficiency than the Ausubel auction, so that there might be a trade-off between these competing objectives for a government seller. There is one anomalous finding in these experiments with two bidders each demanding two units: unit 1 bids in the UPSB auctions exceed those in the sealed-bid Vickrey auction. However, Levin (2005) shows that there is a very appealing lowrevenue (implicitly collusive) Nash equilibrium that is also an ex post equilibrium in which both bidders bid above their private value on unit 1 and zero on their unit 2 bids. Although bidding above value on unit 1 involves a weakly dominated strategy, the collusive outcome is easy to coordinate on, and there is an equitable distribution of payoffs, helping to maintain the collusion.63 Engelbrecht-Wiggans, List, and Reiley

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(2005) show that Levin’s model does not precisely fit the data as, among other things, there are few zero bids on second units. However, Levin noted that this collusive equilibrium collapses once there are 3 or more bidders (with 2 units supplied). This is confirmed in a subsequent experiment with three and five bidders, the results of which show that unit 1 bids in the UPSB auction are statistically indistinguishable from the Vickrey auction (Engelbrecht-Wiggans, List, and Reiley, 2006). Summing Up. UPSB and clock auctions with homogenous goods generate demand reduction, as the theory predicts. But there is substantially more demand reduction and closer-to-equilibrium bidding in the clock auctions. The key mechanism behind this difference appears to be the feedback provided by other bidders’ dropout prices in the clock auction (Kagel and Levin 2001). Ausubel’s version of the dynamic Vickrey auction eliminates much of this demand reduction, with close to equilibrium outcomes (sincere bidding) as well. The SB Vickrey auction generates overbidding relative to induced values, as do unit 1 bids in the UPSB auctions, consistent with the results typically reported for SPSB auctions. All these results hold up both with simulated (computer) bidders and with all human bidders. More generally, these results support the notion that bidding is closer to equilibrium predictions in dynamic auctions with feedback as opposed to SB versions of the same auction mechanism. 3.2 More on Multiunit-Demand Vickrey Auctions Exploration of behavior in multiunit-demand Vickrey auctions also has implications for the mechanism design literature. In single-unit demand auctions, English clock auctions and SPSB auctions are strategically equivalent, with both yielding sincere bidding in weakly dominated strategies. However, in multiunit-demand auctions where bidders have weakly diminishing marginal valuations, the sealed-bid (SB) Vickrey auction and the dynamic Ausubel auction with dropout prices reported are no longer strategically equivalent. Rather, the SB Vickrey auction generates sincere bidding in weakly dominated strategies, whereas the Ausubel auction requires iterated deletion of dominated strategies, a weaker solution concept.64 Nevertheless, Kagel, Kinross, and Levin (KKL, 2001) and Kagel and Levin (2009) show that the Ausubel auction with dropout information generates outcomes much closer to sincere bidding than either the SB Vickrey auction or an Ausubel auction with no dropout information provided (the latter is strategically equivalent to the SB Vickrey auction). While this may not be surprising from a behavioral perspective, it is surprising from a mechanism design perspective, which typically calls for employing a mechanism with the strongest possible solution concept. This suggests a trade-off between the simplicity and transparency of a mechanism and the strength of its solution concept when agents are not fully rational.65 66 In concluding this section, we briefly review results from studies looking at multiunit-demand SB Vickrey auction with complementarities between items, the Vickrey-Clarke-Groves (VCG) mechanism (Vickrey 1961; Clarke 1971; Groves 1973). These are package auctions that permit XOR bids, with bidders bidding for as many packages as they wish, but winning on only one of their bids; for example, in the simple case of two items, A and B, with values VA, VB , and VAB (where VAB is the value of getting both A and B, with VAB > (VA + VB )) with XOR bids, agents are permitted to bid for A alone, for B alone, and for the package containing both A and B but can win only one of the packages bid on. The VCG mechanism is designed to produce sincere bidding and maximum efficiency, using suitably generalized Vickrey

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pricing rules to allocate items. There are a number of technical issues associated with implementing the VCG mechanism as well as potential trade-offs between efficiency and seller revenue that are of concern in using it, discussion of which goes well beyond the scope of the present review (see Ausubel and Milgrom 2006). Rather, our primary interest is to report the results of an experiment applying the SB version of the VCG mechanism. The experiment with the most complicated demand structure investigating the SB VCG mechanism is Chen and Takeuchi (CT; 2010). In each auction bidders compete for 4 items, resulting in a total of 15 possible packages to bid on. Human subjects compete against two computer bidders, who bid sincerely in 1 treatment and randomly in another under 2 different information conditions—with and without information on how the computers were bidding. Sincere bidding is a weakly dominant strategy regardless of what the computers do or the information provided about their bidding strategy. Subjects participated in 10 auctions under each treatment condition. The auction interface automatically computed the value of each of the 15 possible packages so that bidding on all packages was relatively easy. Optimal bidding in this case requires subjects to bid their value on all 15 packages. Subjects consistently failed to do so, with the average frequency of bidding on possible packages going from a low of 65% to 66% for single-item packages to a high of 83% to 86% for combinations of items (83% for the package with all 4 items). This confirms one of the potential concerns with the VCG mechanism (and package-bidding mechanisms in general), the complexity associated with formulating bids for all possible packages of interest. Conditional on making a bid, subjects generally underbid with 57% classified as underbidders, 32% as sincere bidders, and 12% as overbidders. Losing bidders were significantly more likely to increase the number of packages they bid on as well as their bid-to-value ratio in the next auction, with winning bidders decreasing their bid-tovalue ratio (albeit, to a smaller degree than losing bidders). These bid changes indicate that the dominant strategy is not transparent, with subjects adjusting their behavior according to a trial-and-error learning process.67 Remark. The studies reported here have been concerned with behavioral issues within a market design context. In a market design experiment it, is perfectly reasonable for the instructions and working examples to point out the benefits of different bidding strategies in describing how the underlying mechanism works and what it’s supposed to do, which should be considered part of the mechanism. Whether or not this would completely clear up the problems with the SB Vickrey mechanism identified here is problematic as (1). Kagel and Levin (2001) report substantial bidding above value on unit 1 in UPSB auctions with instructions intended to dissuade subjects from doing so, and (2) Kagel, Lein, and Milgrom (2010; reported on in Section 3.3) show that subjects bid on only a small percentage of profitable packages even though they were informed of the benefits of doing so. The key point here is that one part of market design is to identify mechanisms that are aligned closely with agents’ natural tendencies, or educating agents, in order to come closer to achieving a desired outcome. 3.3 Auctions with Synergies Most of the work in this area has been concerned with market design issues, particularly with respect to those raised in the FCC spectrum auctions. Here we cover several small-scale experiments concerned with underlying behavioral issues in the presence of synergies.

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Absent the possibility of package bids, multiunit demand bidders with synergies face an exposure problem. For single-unit demand bidders to win against a multiunitdemand bidder, the sum of what they are willing to pay must beat the larger player’s bid, so that smaller bidders must coordinate their bids to reach the threshold needed to beat the multiunit-demand bidder. However, each small bidder has an incentive to let the other one bid more aggressively in order to get the item at the lowest possible costs. This is referred to as the threshold problem.68 Chernomaz and Levin (CL; 2012) investigate bidding in a highly stylized version of just such an environment. They look at a FPSB auction with and without package bidding. Despite the general preference for iterative auctions, FPSB auctions have been used in a number of cases (Cantillon and Pesendorfer 2007; Epstein et al. 2002), having several attractive features such as their resistance to collusive behavior. CL consider 2 regional bidders, each demanding a single item competing against a global bidder with flat demand for two items. They employ a 2 × 2 experimental design, varying the auction rules (with and without package bidding) and the synergy level (0% and 50%). The two local bidders are restricted to having the same value for their respective items (based on a single random draw), which under the symmetric RNNE should result in the same bids. The global bidders value for winning a single unit is s g , drawn from the same distribution, with the value for winning both units vg = 2βs g , where β represents the synergy value. This highly structured environment permits solving analytically for equilibrium outcomes.69 Among other things, with single-item bidders having the same valuations, under the RNNE there is no exposure problem for the global bidder as he or she either wins both items or loses both. But local bidders still face a threshold problem with package bidding, which, somewhat surprisingly, is present even with no synergies (absent the ability to coordinate their bids, the marginal benefit to single-unit bidders for raising their bids is lower than without package bids). This, in turn, induces the global bidder to bid less, which, in turn, adversely impacts revenue and efficiency. The threshold problem is so strong in this model that sellers using package auctions are predicted to raise substantially less revenue than when selling the items separately under the two synergy levels studied. Changes in revenue are qualitatively consistent with the model because less aggressive bidding with package bidding has a substantial negative effect on revenue. This is primarily driven by the strong response of single-item bidders to the threshold problem, which is much more severe in FPSB auctions given their limited ability to coordinate bids (compared to an ascending-price auction), which induces the global bidder to bid less as well. This, in conjunction with the negligible positive effect of package bids on efficiency when synergies are present, lead CL to sound a cautionary note regarding the efficacy of FPSB auctions in environments such as this. Katok and Roth (2004) also look at auctions with synergies, comparing a descending price (Dutch) auction with an ascending, UP auction. Each auction has three bidders with supply of two homogenous units; one “big” bidder, who has a high value for both items, and two small bidders, who each want one unit. The Dutch auction is, in effect, a package auction since the winner gets to choose how many units to purchase, thereby mitigating the exposure problem (which is very much present in their UP auctions). As already noted, the UP auction mitigates the threshold problem since under the UP rule, no small bidder can obtain a unit at a lower price than the other small bidder. Summary. To date there have been very limited small-scale experimental studies focusing on multiunit demand auctions with synergies.70 The results of these experiments confirm the existence of an exposure problem in the presences of synergies, which

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results in less aggressive bidding, with smaller-than-predicted synergies realized. The introduction of package bidding in CL’s SB auctions introduces significant threshold problems for local bidders. Results from the few VCG package-auction experiments reported at the end of the previous section suggest that this is not a viable alternative to dealing with multiunit demand auctions with synergies, as the frequency of sincere bidding is relatively low and subjects bid on only a small percentage of the packages available (even in auctions with very few items), both of which can severely compromise the promised efficiency gains. Further, the VCG mechanism can result in very low revenue, which is politically unacceptable. Kagel, Lien, and Milgrom (KLM; 2010, 2014) report results comparing a combinatorial clock auction (CCA) mechanism, which permits package bidding with a simultaneous ascending clock auction (SAA) mechanism. They have two regional bidders (demanding multiple units with synergies) competing against a global bidder with demand for all items (with synergies over all items). What is relevant here is: (1) KLM identify a clear threshold problem in some of the CCA auctions. However, the magnitude of the effect was relatively small and in some cases was mitigated by local bidders bidding on packages including items that had zero own value (but positive value to the other local bidder). While rarely getting caught holding any zero-value items, this forces other local bidders to increase their bids if they hope to win any items (Kagel, Lien, and Milgrom 2014). (2) Similar to the results reported in CT for the VGM mechanism with package bidding, subjects bid on only a tiny fraction of the packages available to them even though they were explicitly encouraged to do so and had a computer interface that made placing bids very easy. This package-selection problem underlies inefficiencies in package auctions, because bidders tend to bid on their most profitable packages as well as their “named” packages (i.e., for regional bidders, all the items for which they have positive value and for the global bidder, all items), as the named packages are typically quite profitable. This generates high revenue and efficiency as long as the “named” packages constitute the efficient outcome (i.e., either of the two regional bidders getting all their named items or the global bidder getting all items). However, in cases where the efficient outcome requires that all bidders obtain one or more items or that the items be split between a regional bidder and the global bidder, there are marked reductions in efficiency under the CCA (and relative to the SAA). What drives this last result is that when the named package is no longer the most profitable package, it is often the case that the amount bid on the named package is greater than the bid on the most profitable package (since the latter contains fewer items). This, in conjunction with the CCA auction assigning packages to maximize seller revenue, means that, other things equal, the CCA algorithm would pick a bidder’s named package over the bidder’s most profitable package, which reduces efficiency when the named package no longer coincides with a bidder’s most profitable package. Similar package-selection problems can be found in other multiunit-demand auctions with strong synergies (Brunner et al. 2010; Goeree and Holt 2010; Scheffel, Ziegler, and Bicher 2012). 3.4 Sequential Auctions with Multiunit-Demand Bidders Robert and Montmarquette (RM; 1999) study sequential auctions in which each of 8 bidders have positive demand for mi units, where mi is iid from a Poisson distribution with a maximum mi of 15, and with a total supply of 15 units in each auction. Once mi is determined, the value for each of the mi units is iid from a uniform distribution on

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[0, 100] and ranked in decreasing order for a downward-sloping demand curve for each bidder. RM compare bidding in three types of sequential auctions: Dutch (descendingprice), English (ascending price), and mixed Dutch and English. A round of Dutch auctions was conducted as follows. The first unit was offered at the highest-possible price of 100, with the price lowered by 1 ECU (experimental currency unit) every 2 seconds until a unit was purchased. The second unit was then offered at an initial selling price of 5 ECUs above the winning price for the first item, with this process repeated until all 15 units were sold. Bidders knew when a unit was purchased and the price at which it was purchased. English auctions followed similar rules, with starting prices 5 ECUs below the winning price for the previous unit. In the Dutch-English auctions, the first unit was sold following Dutch auction rules and the second unit was sold using English auction rules, with this process repeated until all units were sold. RM characterize the properties of a symmetric RNNE yielding an efficient allocation for each of the 3 auctions as a reference point against which to evaluate bids. Unfortunately, there is no assurance that the equilibrium identified is unique. However, their model does demonstrate that there are sufficiently rich strategies to induce an efficient allocation in these complicated, multiunit sequential auctions, with the equilibrium outcomes generating the same expected revenue (assuming risk-neutral bidders) across the 3 formats. In addition, the model offers sharp predictions about bidding: In each auction, the winner is the individual with the highest (reindexed) valuation for the unit supplied in that stage, with the price paid for each unit higher (relative to its value) as fewer items remain to be sold. Finally, the theoretical model predicts increasing prices across units sold. In contrast, all 3 auction types had decreasing average prices. Using simulations based on structurally estimated bid functions, RM note that at the start of each auction, the standard deviation associated with the distribution of winning bids is quite large, which initiates a bias pushing winning bids higher than predicted at the beginning of an auction sequence, forcing adjustments later on that are responsible for the declining prices. They suggest that this is the result of the complexity associated with bidding on early units with so many units available to bid on. Brosig and Reiss (BR; 2007) look at the effects of capacity constraints on bidding in sequential auctions.71 They argue that although many real-life auctions run independently of each other, from the point of view of bidders, they form sequences of auctions once capacity considerations are taken into account in procurement auctions or credit constraints are accounted for in ascending price auctions.72 BR’s experimental work focuses on isolating the role of opportunity costs on bids in this sort of environment. They study an IPV auction with two bidders and two consecutive FPSB procurement auctions, where it is common knowledge that bidders have the capacity to undertake only a single project. Bidders learn their own project completion costs for projects A and B (where A is the first project bid on), with both their costs and their competitor’s costs randomly drawn from the same uniform distribution with support [20, 100]. Bids greater than 100 were not accepted. BR employ a 2 × 2 design, varying the nature of the opponent (human or computer rival) and information feedback (no feedback or feedback regarding winners and prices). In all cases, potential bidders on project B know if someone entered and won on project A. Equilibrium outcomes are reasonably complicated in this setup, but most of the key implications are reasonably clear. First, consider a bidder with a cost advantage (lower cost) for project B. The bidder would prefer that the other bidder win project A, since in this event they would be the only bidder on project B, earning 100 − C B (where C B is their cost for completing project B). As such, if they bid on A, they should bid the

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maximum amount, 100. However, a bidder with a cost advantage for project B might decide to skip bidding on A if the cost advantage is large enough. In contrast, bidders with a cost advantage for project A always participate in the first auction as they can potentially earn more than their largest possible payoff in B. Bids in this case are always higher than in a standard single-item-procurement auction since one’s competitor does not always bid on A and submits higher bids than in the single-item case if he or she does participate. Further, conditional on meeting competition when bidding on project B, bids are lower than in the single-item case since it implies that competitor’s completion costs are skewed to the low side, given that he or she skipped bidding on project A. BR’s data show minimal differences in results when competing against human or computerized rivals, with and without information feedback, so the data analysis is pooled over these treatments. The pooled results show that more than 70% of the entry decisions on project A are correct, which is significantly better than an “always enter A” rule. Further, the higher a subject’s expected cost of an incorrect entry, the higher the average frequency of correct entry. As predicted, bids on A are higher than in singleitem (control) auctions. Conditional on C A > C B , close to 77.9% of all bids are exactly at the predicted level of 100, with an additional 12.6% in the interval [99, 100). However, subjects do not appear to correctly update their beliefs about their competitor’s costs according to Bayes’ rule when meeting competition for project B, since, if anything, bids tend to be higher than in the single-item case. Leufkens, Peeters, and Vorsatz (LPV; 2006) consider the impact of positive synergies between items when bidding in a sequential private-value auction. There are two objects for sale in each of the two auctions using a SPSB auction with values iid from a uniform distribution on [0, 100], with the same 4 bidders participating in both auctions. Valuations for the second auction were unknown when bidding in the first auction, but winning the first auction increased the winner’s value in the second auction by a factor s > 1. LPV investigate 3 treatments: a baseline with no synergies (s = 1), one with mild synergies (s = 1.5) and one with strong synergies (s = 2.0). Subjects participated in 50 rounds of 2 auctions each. Their model predicts that with s > 1, all bids in round 1 will be above bidders’ valuations. However, if bidding is symmetric (as assumed), round-one efficiency will not be affected. Their results show that positive synergies reduce round 1 efficiency, with the percentage of auctions won by the high-value holder decreasing from 92.4% to 84.4% to 77.8% for s = 1, 1.5, and 2, respectively. These efficiency reductions are what one would expect given the presence of the exposure problem in conjunction with heterogeneity in bidder-risk preferences. As predicted the larger the synergy factor, the higher bids are above value in round 1, with median overbids of 0.00/4.30/7.0, with s = 1, 1.5, and 2, respectively. They found no statistical support for the prediction that prices would decrease between rounds 1 and 2 in the presence of positive synergies. LPV’s experiment is notable for the introduction of synergies into a sequentialauction framework where predicted outcomes could be solved analytically. The main weakness in their design is that there is huge uncertainty because bidders have no idea what their round 2 values are when bidding in round 1, which creates an unrealistically severe exposure problem for bidders in round 1. This, in turn, may have a strong impact on actual behavior that is not captured by the assumption of risk-neutral bidders. The papers reported on in this section have only begun to scratch the surface with respect to sequential auctions where bidders demand multiple units. This leaves a number of unexplored questions to be investigated.

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IV ADDITIONAL TOPICS 4.1 Collusion in Auctions An issue of enduring concern in auctions is the possibility of collusion. This is not just an intellectual/theoretical exercise because collusion has been identified in a number of cases: Krishna (2002) reports that in the 1980s, 75% of the cartel cases in the United States involving collusion were related to auctions. Klemperer (2002) argues that the issues of primary importance in practical auction design have to do with discouraging collusion, entry deterrence, and predatory behavior. Collusion is a difficult topic to study in the laboratory since it is almost impossible to effectively introduce side payments, and experimental sessions have a natural end point, which is likely to induce some unraveling. Research reviewed in the 1995 survey involved providing subjects with explicit opportunities (even encouragement) to discuss and coordinate bidding strategies. We take up work since then, much of which still focuses on opportunities for bidders to discuss collusive strategies with impunity and nearly all of which involve auctions with multiple units for sale.73 Goswami, Noe, and Rebello (GNR; 1996) look at collusion in multiunit share auctions designed to resemble Treasury bill auctions. They compare the effect of nonbinding preplay communication between bidders in UPSB versus sealed-bid discriminatory auctions. In each auction there were 100 units for sale, with a value of 20 for all bidders. There were 11 bidders in each auction, with bidders specifying the number of units they were willing to purchase at each of 3 possible prices: 10, 15, and 20, with each bidder able to bid up to 100 units. In the class of symmetric, pure strategy, Nash equilibria for the UPSB auction, there exist both a CE and a collusive equilibrium in which bidders extract full surplus from the auction. (There are also a variety of other collusive equilibria without full surplus extraction.) The collusive equilibria do, however, require a great deal of delicate bid coordination. For example, in the most collusive equilibrium, each of the 11 bidders demands 9 units at a price of 20, with all other bids at 10. This strategy profile results in each bidder getting 9 units at the lowest possible price of 10 (with one additional unit assigned randomly). It is easy to see that any unilateral deviation to get a larger share results in raising the price to 20, significantly lowering profits. In the discriminatory auction there is a unique symmetric Nash equilibrium in undominated strategies with all bids at 15. All sessions had at least 12 auctions, with a single set of bidders in each session. In the communication treatments bidders were allowed to speak to each other in between every other round. Following each auction bidders were told the actual market clearing price, their own allocation and their own payoff. There were essentially no differences in clearing prices between the discriminatory auctions with and without communication: none cleared at the lowest price of 10, with 65% clearing at 15 without communication versus 69% with communication (with the remainder clearing at 20). In contrast, in the UPSB auctions with communication, 36% cleared at 10 versus 0% without, and another 30% cleared at 15 with communication versus 16% without. As such, average prices were substantially lower in the UPSB auctions with communication than without, with no difference with and without communication for the discriminatory auctions. Naïve collusive outcomes predominated; for example, all bidders agreeing to place all bids at 10, as opposed to the rather elaborate selfenforcing collusive Nash equilibrium. The results suggest that UPSB share auctions are more susceptible to collusion than discriminatory share auctions.

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Sade, Schnitzlein, and Zender (SSZ; 2006) conduct an experiment similar to GNRs but with different results, as average revenue is quite similar between the discriminatory and UPSB formats. One key difference between SSZ and GNR is that in SSZ there were 4 possible prices of 17, 18, 19, and 20 versus 3 possible prices of 10, 15, and 20 in GNR. Thus, there were fewer alternatives to coordinate on in GNR and the potential profits from collusion were substantially higher in GNR, both of which would tend to promote collusion. One interesting sidelight of the SSZ experiment is their use of both students and finance industry professionals, with the professionals generating higher average revenue (lower earnings) than the students, even though they had the same opportunities to collude. Regulations precluded cash payments to the professionals, so they were rewarded with prizes bearing the logos of the sponsoring universities. As such, “winning” might have been more salient for the professionals. Phillips, Menkhaus, and Coatney (PMC; 2003) study collusion in a series of sequential English auctions designed to mimic livestock auctions.74 Several facilitating practices were employed: the same set of bidders over a series of 7 auctions, knowledge about the number of units for sale, and communication via an online chat program. They investigate auctions with 6 and 2 bidders and between 19 and 30 (homogenous) units for sale in any given auction. Bidders had identical negatively sloped demand curves, with a reservation price set 20 points below the average price had all units been sold to the highest value bidders at their induced values. Collusion increased with bidder experience, so we focus on bidding in the last auction in each session. The 6-bidder control treatment yields average prices at 77% of a norm in which each unit is sold at its valuation, going from the highest to lowest value. Communication, with or without bidder identification, reduced average prices to between 50% and 52% of this norm. These lower prices were accomplished primarily through bid-rotation rules that communication facilitated. Further, while there was some cheating over the last several units in each set of auctions, it did not destroy effective rotation in subsequent auctions and/or lead to substantial unraveling in the last auction (see Figure 9.12). Information about quantity for sale had no impact compared to the control treatment. The baseline treatment with 2 bidders had average prices at 75% of the norm in which each unit is sold at its valuation. Communication reduced average prices to 58% of this norm. Unlike the 6-bidder auctions, information about quantity for sale without any opportunity for communication had almost the same effect as communication with average prices at 61% of the norm. PMC, using the chat records for support, suggest that the somewhat smaller effect of communication in the 2-buyer auctions resulted from disputes as bidders compared their relative gains, whereas it was too difficult to go beyond a simple bid-rotation rule in the 6-buyer case. Note that collusion might have been even more effective in this study had there been no reserve price in place. Further, as a subsequent paper shows (Phillips and Menkhaus 2009), in seller-active auctions (where live sellers replace the experimenter), the number of units supplied varies widely between auctions, significantly disrupting the collusive effect of a constant supply with small numbers of buyers. It remains to be seen if this would have a similar effect when small numbers of buyers are allowed to communicate. Kwasnica and Sherstyuk (KS; 2007) look at collusion in simultaneous ascending price multiunit demand (SAA) auctions. The experiment is inspired by Brusco and Lopomo (BL; 2002), who show that there exist collusive Nash equilibria in SAA auctions in which bidders start bidding on their highest-valued item and, if there are no competing bids, stop bidding. This equilibrium is supported by the threat of competition and higher

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prices if rivals do not cooperate.75 Although this equilibrium does not require repeated interactions with the same set of bidders, KS look for it in a repeated-play setting as (1) this adds collusive opportunities via bid rotation to the strategy set and is more relevant to many auction settings outside the lab, and (2) it is no doubt substantially more difficult to achieve BL style collusion in one-shot games.76 Their experimental design involved two objects for sale, with complementarities between items in some sessions, along with an uncertain end point and no opportunity for discussions between bidders. In the no-complements case they define collusion as occurring with prices below 50% of the CE. For auctions with complements they define collusive bidding when both items are awarded to the bidder with the highest value for the package, at a price equal to the second-highest valuation. (This standard for complements is more problematic since bidders face an exposure problem, which in and of itself may prevent an efficient allocation.) KS’s strongest results are in auctions with two bidders: Absent complements 10% of the auctions with inexperienced bidders, and 55% with experienced bidders, are classified as collusive, with a number of auctions following the BL mechanism for

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tacit collusion. Collusion was reasonably frequent in markets with two bidders and modest complements, averaging 31% of all auctions with inexperienced subjects. But it was much less common with larger complementarities: 0 out of 16 auctions with inexperienced subjects and 2 out of 11 auctions with experienced subjects.77 In contrast, none of their 5 bidder auctions were collusive, regardless of bidder experience and the presence or absence of complements. Li and Plott (LP; 2009) study collusion in multiunit-demand SAA auctions with 8 bidders and 8 items. Their strategy is to induce collusion by using an “incubator” technology and then study factors capable of mitigating the collusion. Their incubator technology involves: (1) bidders valuations being “aligned” and “folded” so that each pair of bidders has a unique item they value the most, with bidder i ’s second-highestvalued item very close to bidder j ’s highest-valued item, and vice versa (in this way it’s easy for a bidder to retaliate should his or her closest rival compete for his or her highestvalued item). Also (2) there is complete information about all bidders’ valuations, and (3) the same set of bidders competes over several auctions with an unknown end point (but no opportunities for discussion between rivals). Under these conditions there exists a collusive Nash equilibrium of the sort specified in BL, as well as a Nash equilibrium with competitive prices. Once collusion is established, LP explore several remedies including (1) dropping bidder identification, (2) removing information about rivals values, (3) using a fixed end point for the auction as opposed to a soft ending (bidding continues until no new bids are entered for 30 seconds), (4) removing several items for sale (thus increasing competitive pressure), and (5) changing bidders’ expectations by having some pairs of bidders with the highest value for the same item. Remedies 1–3 alone had minimal impact. Adding remedy 5 to 1–3 reliably broke up collusion, with competitive outcomes continuing after the aligned and folded preference structure was reinstated (but not announced).78 Offerman and Potters (OP; 2006) look at whether auctioning of entry licenses induces collusion in the product market. Standard economic arguments hold that entry fees constitute a sunk cost, so should have no effect on pricing in the product market. However, many companies claim that they will have to charge higher prices in the product market in order to recoup entry fees. In addition, OP note that if entry rights are auctioned off, this will result in selecting bidders with the highest profit expectations in the product market, which might foster tacit collusion. OP employ a product market with price-setting duopolists with differentiated products, with a unique stage-game Nash equilibrium in which each duopolist charges a price of 60 ECUs and earns a profit of 5,000 in each period. This compares with the joint profit-maximizing collusive outcome, with both firms charging 150 and earning profits of 9,000.79 Subjects received feedback following each period about their own and their opponent’s price, quantity, revenue, cost, and profit but were not allowed to discuss strategies. There were three treatments: (1) an auction treatment, in which 4 subjects bid for entry rights, with the 2 highest bidders entering and paying what they bid, (2) a fixed-cost treatment where the entry rights were randomly assigned at an exogenously determined entry fee comparable to fees in the auction treatment, and (3) a baseline treatment in which the entry rights were assigned randomly with no entry fees. In all 3 treatments, subjects first played the duopoly game for 10 periods against the same opponent. After that, each subject was randomly assigned to a group of 4, which included their rival from the duopoly game. These groups remained fixed until the end of the experiment (20 more periods) with entry licenses, valid for 5 periods, auctioned

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off at the start of each block of 5 periods. Players without entry licenses received a fixed payment of 1000 per period, compared to expected earnings of 5000 in the (competitive) stage game Nash equilibrium. Figure 9.13 shows average prices in periods 1–10, which were approximately the same before the 3 entry treatments were introduced. In the first of the two 5-period blocks with entry (periods 11–20), average prices were significantly higher in both the auction and fixed-cost treatments compared to the baseline treatment ( p < 0.10) but not significantly different from each other. These differences from the baseline treatment were much less pronounced in the last 10 entry periods and were no longer statistically significant ( p > 0.10). Average winning bids were close to 20,000, the net expected profit from the stage-game Nash equilibrium following entry. The role of entry fees in fostering collusion is supported by Spearman rank-order correlations between entry fees and average prices, which were positive and statistically significant at the 10% level in periods 11–20 for the auction treatment ( p = 0.14 for the fixed-cost treatment) and significant at the 5% level or better for both treatments in periods 21–30. Finally, the data show that collusion is “clustered,” so that some groups had prices close to the stage-game Nash equilibrium, while others set prices at higher levels. As such it would be more accurate to say that entry fees increased the probability of collusion than that they increased the degree of collusion.80 Further, the similarity in outcomes between the auction treatment and the fixed-cost treatment would support industry arguments that entry fees by themselves will lead to higher prices (via tacit collusion) in concentrated industries. Summary. All the auctions considered here involved the same set of subjects competing in a series of auctions, usually with an unannounced end point. Repetition with the same cohort appears to be a key facilitating factor, a factor likely to be at play in field settings. Communication between bidders reliably facilitates collusion, which seems hardly surprising. However, Whinston (2006) notes there is little in formal economic theory about the way in which prohibitions on (nonbinding) price agreements prevent anticompetitive prices, with the published empirical work offering surprisingly little evidence that preventing oligopolists from talking has a substantial effect on prices

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charged. In contrast, the experimental data show quite strong effects when certain facilitating practices are in place. Sealed-bid discriminatory auctions are more collusion proof than ascending price auctions which provide easier opportunities to detect and punish non-cooperators. Competitive pressures seem to play a role as well, as suggested by the role played in breaking up collusion in LP.81 4.2 Bidder’s Choice Auctions: Creating Competition Out of Thin Air The National Association of Realtors defines a bidders’ choice auction as82 A method of sale whereby the successful high bidder wins the right to choose a property (or properties) from a grouping of similar or like-kind properties. After the high bidder’s selection, the property is deleted from the group, and the second round of bidding commences, with the high bidder in round two choosing a property which is then deleted from the group and so on, until all properties are sold.

This type of bidding is very popular when selling time-shares, condominiums, and building lots. Goree, Plott, and Wooders (GPW; 2004) were the first to study this auction mechanism experimentally, noting that it can create competition between bidders who are interested in different items. They illustrate this with the following example: Consider the case of two bidders and two items, with each bidder interested in a different item. In a standard SAA, revenue is zero when bidders prefer different items, which occurs with probability 0.50. In contrast, in the first stage of an ascending-price rightto-choose (ARTC) auction, there is always competition since bidders, not knowing their rival’s preferences, run the risk that the stage 1 winner will take their preferred item. GPW show that if bidders are risk neutral, the ARTC will raise the same average revenue as the SAA, but if they are risk averse, the ARTC will raise more revenue, which may account for its popularity. In GPW there are 4 bidders in each auction, with 2 items for sale, A and B. Each bidder had a 50% chance that either item A or B (but not both) will be his or her “preferred item,” drawn iid from a uniform distribution.83 The value for their nonpreferred item was effectively zero, so that each bidder had positive value for only one of the two items in any given auction (zero substitution possibilities between items). In the ARTC, after the first item was sold, bidders observed the item chosen, with the remaining item sold in an ascending-price auction. In the SAA, items were sold simultaneously through two ascending-price auctions, with bidders restricted to bidding in only one of the two auctions at any given time. Revenues were 19.3% higher in the ARTC than in the SAA, with 100% efficiency in the SAA versus 98.4% efficiency in the ARTC. The estimated coefficient of relative risk aversion, 1 − r , is 0.39, consistent with the higher revenues in the ARTC. Eliaz, Offerman, and Schotter (EOS; 2008) studied an RTC auction with 4 different items for sale, with 2 buyers valuing each item, and with zero substitution possibilities between items. In the RTC auction, 8 buyers participated in a SPSB auction in which the winner had the right to pick which item he or she wanted, paying the second-highest bid price from among the 8 bids submitted. The item selected was announced so that the other buyer interested in that particular item exits the auction. This process repeated itself with the remaining bidders until all 4 items were sold. The control treatment involved 4 separate good-by-good (GBG) auctions, in which the 2 bidders interested in each item compete in 4 separate SPSB auctions. Two GBG treatments were employed, one with no minimum bid requirement and one with a revenue maximizing minimum

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bid requirement. With risk-neutral bidders, expected revenue is the same between the RTC and GBG (with no minimum-bid requirement), with risk aversion generating higher expected revenue in the RTC auction. The RTC auctions raised significantly more revenue than either the unrestricted or optimal GBG formats (40.4% and 13.9% higher revenue, respectively). Average efficiency was comparable between the RTC and unrestricted GBG auctions (98.2% versus 98.3%) and higher than in the optimal GBG auctions (87.9%). To determine whether risk aversion was the source of the higher revenue in the RTC auctions, EOS employed a no-information RTC (NIRTC) auction where, after each phase, bidders were not informed as to which item was sold and losing bidders were not eliminated from the auction. As a result, following the first item sold, buyers are essentially bidding in a SPSB auction in which the high bidder wins a lottery that awards him or her their most preferred good with positive probability, and wins a zero-value item with the complementary probability. Risk-neutral buyers will bid their expected value for their positively-valued item, but risk-averse bidders will bid strictly less than the expected value of the item. Assuming homogeneous risk-averse bidders, the RTC auction with risk aversion provides a better fit to the data than assuming risk neutrality. However, the NIRTC auction with risk aversion provides a worse fit to the data. Thus, EOS reject risk aversion as the key factor behind higher revenue in RTC auctions. Rather, their preferred explanation rests on probability (mis-) weighting, with subjects acting as if they face fiercer competition than they actually do. Salmon and Iachini (SI; 2007) examine a “pooled” RTC auction, with a number of similarities to the NIRTC auctions in EOS. They conduct a discriminatory sealed-bid auction with multiple units for sale, with all bidders submitting a single bid at the same time. Bidders’ values are perfectly correlated across items, so that each bidder has the exact same ordinal ranking across items. (Think of selling several condominiums in a given building, each of which is ranked from highest to lowest based on its scenic view. But because of the location of the building relative to where bidders work, bidder i ranks each apartment uniformly higher than bidder j .) Thus, unlike the other RTC auctions reported on, there are some substitution possibilities between items, albeit with common ordinal preferences over the goods. Bids are ranked from highest to lowest, with the high bidder getting first choice, the second-highest bidder getting second choice, and so on, with all winners paying what they bid. Following Menezes and Monteiro (1998), assuming symmetric bidding strategies, SI solve for bid functions numerically for both risk-neutral and loss-averse bidders.84 Loss aversion is relevant here since bidders can lose money when bidding according to the RNNE, as a bid designed to get a higher-valued unit may end up securing a unit with a lower value, with bidders paying what they bid. They compare outcomes in the pooled RTC auctions to an SAA in which subjects are restricted to holding the high bid on one item at a time.85 Their results show that revenue is uniformly, and substantially, higher in the pooled RTC auctions than in the SAA (41.8% higher), well above the revenue predicted under the RNNE for the RTC auctions. In fact, bidders suffer persistent losses, so that bidder profits are well below those in the SAA. Efficiency is essentially the same between the two auction formats, averaging around 95% in both cases. Looking at individual bids in the RTC auction, their shape is essentially the same as the theory predicts, but bid functions are displaced upward relative to risk neutrality. SI explore a number of alternative explanations for this upward displacement of the bid functions, with their preferred explanation consisting of a probability (mis-) weighting model: in this case “attentional”

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bias, whereby bidders focus most of their attention on winning their most preferred 2 or 3 units in the auction, largely ignoring the possibility of being “stuck” with lowervalued units. Finally, SI note that assuming their results translate outside the laboratory, the kind of pooled auction format they employ would have trouble sustaining itself, as persistent losses would reduce incentives to bid, as well as winning bidders defaulting on their bids. Summary. The three RTC experiments reported on provide strong evidence for their revenue-raising ability compared to either an SAA or a GBG format. The results reported in EOS and SI lie totally outside what theory predicts. The losses associated with the pooled RTC auctions in SI would seem to limit their use in field settings. The total lack of substitutability between commodities in the GPW and EOS experiments seems unrealistic for the situations these auctions are intended to represent. Thus, there is scope to explore either an ascending, or sequential, RTC auction in which bidders demand a single unit, but the items have some degree of substitutable, comparing outcomes to either an SAA or GBG auction. Nevertheless, the results of these three experiments are an exciting new application of experimental methodology designed to better understand the basis for RTC auctions found in field settings. On a theoretical level, both EOS and SI attribute the higher-than-predicted revenue to bidders systematically misweighting probabilities of one sort or another, which ties back to results reported earlier (Section 1.1) on bidding above the RNNE in FPSB auctions. 4.3 Internet Auctions Internet auctions provide new opportunities to conduct experiments, with considerable potential for applications.86 Lucking-Reiley (LR; 1999) used the Internet to sell collectable trading cards under the 4 standard auction formats (Dutch, English, FPSB, and SPSB auctions), investigating the revenue equivalence theorem. He finds that Dutch auctions produce 30% higher revenue than FPSB auctions, a reversal of previous laboratory results, and that English and SPSB auctions produce roughly the same revenue. These results are interesting but lack the controls present in more standard laboratory experiments; that is, there may well be a common value element to the trading cards, and Dutch auctions provide an opportunity to use the game cards immediately, which cannot be done until the fixed closing time in the FPSB auctions. eBay auctions have a fixed closing time, with many bidders submitting bids just seconds before the closing time (sniping), while others increase their bids over time in response to higher bids. In contrast, Amazon auctions automatically extend the closing time in response to late bids (“soft” closing), with much less last-minute bidding than in comparable eBay auctions. These differences raise two questions addressed by Roth and Ockenfels (RO; 2002): (1) Why are there sharp differences in last-minute bidding between the two auction designs? (2) Since eBay has a number of characteristics similar to a standard SPSB auction, why is there increased bidding by the same bidder over time? RO suggest several (rational) reasons for sniping in (essentially) private value eBay auctions with their fixed deadline: (1) implicit collusion on the part of snipers in an effort to get the item at rock bottom prices, since congestion will result in some of the lastminute bids not being recorded at the Web site and/or (2) a best response to incremental bidding on the part of less sophisticated bidders in an effort to avert a bidding war. In contrast, sniping for items with a significant CV component could result from (1)

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better-informed bidders’ efforts to conceal their superior information on high-valued collectables and/or (2) bidders updating their valuation of items as bids come in. Because there are a number of other differences between eBay and Amazon than their ending rules, as well as the difficulty of clearly distinguishing between private-value and CV auctions in field settings, Ariely, Ockenfels, and Roth (AOR; 2005) conduct a laboratory experiment in which the only difference between auction institutions is the ending rule for private-value goods—an eBay style auction with either a 0.8 or 1.0 probability that a late bid will be accepted, and an Amazon-style auction with a 0.8 probability that a late bid will be accepted, in which case the auction is automatically extended for a fixed time period. Their results show quite clearly that there is more late bidding in both of their eBay auction treatments compared to the Amazon auction. Further, there is significantly more late bidding in the eBay treatment where last-minute bids would be recorded with probability 1 than with probability 0.8. This rules out tacit collusion as the only basis for sniping and more than likely represents, at least in part, best responding to incremental bidding on the part of less sophisticated bidders. Ely and Hossain (2009) compare sniping with “squatting” (a single early bid) in a series of eBay auctions (actual bids they made for recently released movie DVDs). Their experiment represents an attempt to look at more general equilibrium effects of sniping versus the alternative of squatting. They corroborate that sniping is a best response to naïve bidding of the sort studied in AOR. But sniping does not lead to large increases in surplus in their experiment because of multiple eBay auctions for the same item, so that early bids (squatting) deter entry into those particular auctions. At the same time they recognize that sniping would be more effective if, instead of being done randomly, as in their experiment, it was directed at eBay auctions with the lowest standing bid. Salmon and Wilson (2008) investigate the practice of second-chance offers to nonwinning bidders in Internet auctions when selling multiple (identical) items. They compare a two-stage game with a SPSB auction followed by an ultimatum game between the seller and the second-highest bidder versus selling the two items in a sequential English auction. As predicted, the auction-ultimatum-game mechanism generates more revenue than the sequential English auction, providing a potential explanation for the practice of second-chance offers to losing bidders. Shahriar and Wooders (SW; 2011) study “buy-it-now” (BIN) options popular in eBay, Yahoo, and other Internet auctions.87 They employ an English clock auction (with a soft close) and a BIN price that must be exercised prior to the start of the auction. For a private value auction when bidders are risk averse, Reynolds and Wooders (RW; 2009) show that a suitably chosen BIN will raise revenue as it extracts a risk premium from bidders wishing to avoid uncertainty over winning and the price paid. In contrast, for common value auctions, if bidders are sophisticated and do not suffer from a WC, RW show that a BIN will not raise revenue, or be exercised, for risk-neutral or risk-averse bidders who do not suffer from a winner’s curse. SW’s results support the risk-aversion predictions for the private values case, as auctions with a BIN option raised average revenue 6.8% compared to the control treatment and 11.9% conditional on the BIN being accepted, which occurred in 45% of the auctions. Introducing a BIN that is a little above the (unconditional) expected value of the item in an ascending-price CV auction raises revenue by 4.2%, but consistent with a WC is exercised in 78.9% of the auctions. Further, bidders tend to drop out earlier when the BIN was not accepted compared to controls, even though rejection of the BIN is, in theory, completely uninformative. SW explain these anomalous results through an extension of the naïve bidding model developed in Kagel and Levin (1986), in which

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bidders make no adjustment to the adverse selection effect conditional on winning the item, falling prey to the WC.88 4.4 Entry into Auctions Most of the theoretical literature on auctions treat the number of bidders, N, as fixed. The fixed-N paradigm simplifies the analysis and allows for easy comparisons of revenue and efficiency between different auctions mechanisms and is an essential assumption underlying the revenue equivalence theorem. The key motivation for looking at endogenous entry is that it’s both costly and time consuming to prepare bids so that it is part and parcel of the auction process. As such, it should not be swept under the rug by assuming an exogenously determined number of entrants. Further, casual observation shows that the number of bidders in similar auctions can vary substantially, leaving the impression that it is governed by a stochastic, rather than a deterministic, process. A natural question, both theoretically and experimentally, is how sensitive are the typical auction results to dropping the fixed-N assumption, as opposed to allowing for endogenous entry.89 There have been two main approaches to modeling auctions with entry.90 Both start by assuming N potential entrants and an entry cost, c (e.g., bid-preparation costs), since otherwise all potential bidders enter and we are back to a fixed-N setup. The first approach assumes that bidders learn their private information signals only after incurring the entry cost. In this case the theory has focused on two types of equilibria. The first is a deterministic, asymmetric equilibrium in which bidders use pure entry strategies with exactly n∗ bidders, the number of bidders that can profitably enter the auction. The remaining (N − n∗ ) bidders remain out and have no further impact on the auction (see Smith 1982, 1984; Engelbrecht-Wiggans, 1987, 1993; and McAfee and McMillan 1987). The second model, (Levin and Smith (LS) 1994) is stochastic with a unique symmetric mixed-strategy equilibrium determining a probability of entry, q ∗ , which leaves all bidders just indifferent between entering and staying out. This results in entry being a random variable that is governed by a binomial distribution with N and q ∗ as the two parameters, with q ∗ depending on the expected rewards from entry relative to its cost, q ∗ = Q ∗ (c, N).91 We refer to the first equilibrium as “deterministic” and to the second as “stochastic.” A second modeling approach is to assume that the N potential bidders obtain information about their type before they decide to enter. This approach generates a unique pure strategy equilibrium characterized by a cutoff value, which is a function of a bidders’ type, which determines who enters and who stays out (see, for example, Palfrey and Pevnitskaya 2008). Here, the realized number of entrants is a random variable governed by a binomial distribution with N and q ∗ , where q ∗ in this case represents the probability of a player’s type exceeding the cutoff level. Smith and Levin (SL; 2001) conduct an experiment investigating their stochastic bidding model’s predictions. The experiment focuses on entry decisions. To simply things, subjects are provided with a table giving them payoffs conditional on the number of subjects choosing to “enter” an auction. That is, there is no bidding phase, just a decision to enter or not given different, exogenously determined, opportunity costs of entry. This reduces the experiment to a coordination game based on the expected returns for an IPV auction with n∗ bidders entering the auction.92 Before each period, the number of potential entrants, N, the cost of entering, c, and the schedule of (decreasing) payoffs conditional on n∗ entering were publicly announced. Subjects received feedback regarding the total number of entrants and earnings after each round

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of play. There were two treatments, one N = 4 and one with a larger number of potential entrants (N = 8), with four different costs of entry within each treatment. At each cost level, there was room for “profitable” entry by at least 1 bidder but not more than 3 bidders. The aggregate data are consistent with the stochastic entry model because of the following. (1) On average, more subjects entered the market under each of the treatment conditions than predicted under the deterministic asymmetric equilibrium. (2) There are numerous (and substantial) deviations from n∗ , sometimes with “too many” bidders entering and sometimes “too few.” (3) At each of the cost levels, with sufficient numbers of observations to perform exact tests, SL are unable to reject a null hypothesis that the average decrease in entry rates is significantly different from those predicted under the risk neutral stochastic model. (4) Consistent with the stochastic models prediction that average expected profits will be driven to zero, profits for entrants, relative to what they could have earned by staying out, averaged −$0.02 per subject, per period, over all auctions. (5) Simulations show that the stochastic model’s prediction that the total surplus generated in the auction will decrease when the number of potential entrants’ increases is satisfied for all entry costs, with the reduction in surplus particularly strong at the highest entry cost ($4.00). This provides empirical support for one of the most intriguing policy implications of the stochastic model: other things equal, thicker markets are less efficient due to increased costs of entry, so that society may benefit from appropriately designed measures to limit the number of potential bidders. While the preceding shows that the stochastic model organizes the aggregate data rather well, there were some significant deviations at the individual subject level. The stochastic model assumes that bidders are symmetric, which implies that for each treatment they all employ the same (symmetric) entry probability. The data soundly reject this. Among inexperienced subjects, this hypothesis is rejected 26% of the time and 33% of the time for experienced subjects. The failure to find a uniform probability of entry across all subjects, corresponds to failures commonly reported in other coordination games (Ochs 1995), pointing to the need for further research to identify a more accurate, stochastic asymmetric entry model. The main weakness of the LS model is that its symmetric equilibrium uses a mixed strategy. When the N potential bidders are risk neutral or symmetrically risk averse, a mixed-strategy equilibrium is unavoidable. Palfrey and Pevnitskaya (PP; 2008) purify the mixed-strategy equilibrium by assuming that the number of potential entrants, N, are drawn from a population with heterogeneous (homegrown) risk preferences. As such, there is a critical level of risk aversion (the cutoff level) for which bidders who are more risk averse select to stay out in order to avoid entry costs, while the less risk averse enter. PP explore an environment with either 4 or 6 potential bidders in an IPV FPSB auction. Sessions with no entry costs and fixed numbers of bidders served as the control treatment. Parameter values were adjusted in such a way that the RNNE entry probability, q ∗ , was either 0.5 or 0.35, representing high and low anticipated entry rates. Bidders’ types, needed to purify the mixed-strategy equilibrium, are determined by their (homegrown) risk preferences, with bidders who are more risk tolerant entering the auction, after which they learn their value for the item. Comparing auctions with endogenous versus exogenous entry, as predicted the estimated slopes of the bid functions are smaller with endogenous entry in 11 out of 12 cases, consistent with the prediction that with endogenous entry, the more risk-averse subjects choose to stay out of the auction. Further, comparing estimated slopes of bid

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functions for different realized values of n, slopes are larger with q ∗ = 0.5 than 0.35 in all cases, again consistent with the prediction that with higher entry rates, more riskaverse bidders enter the auctions, resulting in more aggressive bidding. PP conclude that subjects who enter the auction are, on average, less risk averse than those who stay out. However, entry rates were consistently higher than the RNNE, indicating excess entry and resulting in average profits for entrants that were substantially and consistently lower than the outside option (approximately 50% less). One potential source of this excess entry is that not entering is boring, with entering providing some entertainment value. To test this, PP employ a treatment in which nonentrants have the opportunity to play a simple computer game. While the average entry rate declined significantly, from 0.61 to 0.54 (with q ∗ = 0.50), it was still significantly above the predicted upper bound for entry. One important difference between this experiment and SL who got close to risk-neutral entry rates is that potential entrants were better informed about the expected value of entering versus staying out in SL (due to the fact that entrants were informed of the expected payoff for entry, as there was no actual bidding). The importance of clear information concerning expected profits will be shown in the next experiment reported on here. Finally, the most direct test of the cutoff entry model would be to examine individual subject behavior: do the same least risk-averse subjects almost always enter under the same treatment conditions? Unfortunately, the authors do not provide these data. Ivanova-Stenzel and Salmon (ISS; 2008) compare bidding in a FPSB auction with an English clock auction when bidders have a choice as to which auction to enter. That is, they take endogenous entry to its logical conclusion by having bidders choose which of two different auction formats to bid in. In this case the cost of entry is the opportunity cost of participating in the other auction. The key question posed is whether revenue equivalence can be restored through competition between auction formats. Bidders first participated in a “learning phase,” where they bid in both the clock auction and the FPSB auction with exogenously determined numbers of bidders, providing subjects with experience with both auction formats. Further, to ensure that bidders knew the likely payoffs from the two formats, at the end of the learning phase they received feedback regarding the sessionwide average profit for each format for all values of n. In the second phase subjects split into two groups of 6 bidders each and proceeded to bid in 30 rounds of auctions, choosing in which auction to participate.93 Their main result is that the clock auctions attracted more bidders than the FPSB auctions, so that average revenue was essentially the same in both formats, as was average efficiency. ISS conclude that the key result in their study is not the approximate revenue equivalence, but rather that revenue in the English auctions increases sufficiently with endogenous entry to offset the increase in revenue in the FPSB auctions resulting from the consistent bidding above the RNNE. Several other entry-related studies are worth mentioning. Goeree and others (2013) study multiunit demand auctions when two incumbent firms face a potential negative externality in the form of a new entrant, who, if winning items, will compete in the resulting product market.94 Their paper compares entry rates in a UP clock auction with that of a SB discriminatory auction. Their results show that both auction formats induced similar high levels of entry. However, the mechanism behind the entry rates differed between the two auctions: In the ascending price auctions, entry levels are between those predicted by the preemptive equilibrium, in which incumbents completely block entry, and the demand-reduction equilibrium, in which at least one of the incumbents always permits entry. In the discriminatory auctions, there is more entry

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than predicted because of incumbents’ failure to coordinate their bids to deter entry. As a result, potential entrants’ prospects for successfully entering the market were similar between the two formats.95 Kagel, Pevnitskaya, and Ye (KPY; 2008) look at entry in markets with indicative bidding. Indicative bidding is a two-stage process sometimes used in the sale of business assets with very high values. In the first stage the auctioneer solicits a large group of interested buyers to submit nonbinding bids, with the highest of these nonbinding bids used to establish a short list of final (second-stage) bidders. These short-listed bidders then engage in extensive studies to acquire more information about the asset for sale, after which they submit firm and final bids (typically in a FPSB auction). Ye (2004) shows that there does not exist a symmetric increasing equilibrium with indicative bidding. As a result, the most qualified bidders may not be on the short list, which may result in substantial efficiency losses. In contrast, there are a number of alternative twostage bidding procedures that, in theory at least, guarantee that the short list consists of those bidders with the highest preliminary (first-stage) valuations, while preserving the best properties of indicative bidding—namely, avoidance of the costly asset valuation process for all but the short-listed bidders. This is the type of situation tailor-made for an experiment, since there is no guarantee that the alternatives to indicative bidding will produce fully efficient outcomes, nor is there any other way to evaluate the efficiency losses associated with indicative bidding. KPY’s results show that indicative bidding performs as well as a uniform-price sealed-bid (UPSB) auction in terms of those bidders with the highest first-stage valuations gaining entry into stage 2. This is a result of (1) sufficient heterogeneity in firststage bids under the UPSB auctions, so that entry is not 100% efficient as predicted and (2) first-stage bids under indicative bidding being highly correlated with firststage values, resulting in highly efficient entry. The latter is reflective of the fact that bidders with low first-stage values lost money, on average, as a result of entry, while those with higher valuations consistently earned positive profits. Further, indicative bidding does better on other dimensions because it yields higher average profits and fewer bankruptcies in the initial auction periods due to systematic overbidding in the UPSB auctions. Although these higher revenues are good for sellers in the short run, they would more than likely destroy its long-run viability. KPY report similar problems with a discriminatory first-stage auction. These results suggest a trade-off between types of mechanisms: one with clear equilibrium predictions ensuring efficiency in theory but involving relatively complex rules and calculations for bidders, the other with no clear equilibrium prediction but with relatively simple rules. The results are similar to those reported in KL (2010) for multiunit-demand Vickrey-type auctions, where a mechanism with a weaker solution concept achieves higher efficiency than one with a stronger solution concept due to its relative transparency (see Section 3.2). Goeree, Offerman, and Schram (GOS; 2006) compare revenue between FPSB auctions versus simultaneous ascending auctions (SAA) for selling heterogeneous licenses under a market structure, mimicking the 2002 Dutch sale of airwave-rights auctions, a market with strong incumbents and relatively weak potential entrants. The key question addressed in this relatively uncompetitive situation is whether a FPSB auction would be more attractive to potential entrants than an ascending price auction, thereby generating more revenue and a more competitive aftermarket. Klemperer (2002) predicts this outcome on the grounds that the uncertainty inherent in the SB format encourages incumbent (strong) bidders to shave their bids less, while the ascending auction format

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discourages entrants as strong bidders simply “trail” weaker ones, overbidding them by the minimum amount required until they drop out. GOS confirm Klemperer’s concerns, as in auctions with endogenous entry of weak bidders, their probability of winning was higher, and their rate of entry was higher in the FPSB auctions.96 However, revenue was essentially the same between the two auction formats as was efficiency.

5 SUMMARY AND CONCLUSIONS Experimental research in auctions has continued along with the extensive theoretical work on auctions since the appearance of Kagel’s survey in The Handbook of Experimental Economics in 1995. Results reported in the original 1995 survey focused on the revenue equivalence theorem and initial investigations of the winner’s curse, so they could be easily summarized. In contrast, it is impossible to summarize the work reported on here in a few sentences, given the much broader scope of the issues covered since 1995. We anticipate a continued flow of auction experiments given the many applications of auctions: privatization of government assets, the continued growth of online and business-to-business auctions, and theorists’ attempts to better understand the many variations in auction design in practice and to design better auction institutions.

ACKNOWLEDGMENTS Research support from the National Science Foundation for our experimental auction work is gratefully acknowledged. We thank Tim Cason, Sonsino Doron, Dirk Engelmann, Charles Holt, Radsoveta Ivanova-Stenzel, Julian Jameson, John List, Eric Maskin, Axel Ockenfels, Paul Pezanis-Christou, Ronald Peters, Tim Salmon, and participants at the Stony Brook Game Theory Festival and the Harvard Conference on the Handbook of Experimental Economics, Volume 2, for helpful comments and suggestions on earlier drafts of this survey. Any opinions, findings, conclusions, or recommendations in this material are those of the authors and do not necessarily reflect the views of the National Science Foundation.

NOTES 1. The Dutch auction starts with a high price, which is lowered until a bidder accepts at that price. In English auctions price starts low and increases until only one bidder remains active, paying the price at which the next to last bidder dropped out. In a first- (second-) price sealed-bid auction, the high bidder wins the item and pays the highest (second-highest) bid. 2. These experiments use computerized rivals who bid according to the RNNE bidding strategy in the firstprice sealed-bid auctions. This permits isolating the risk preferences of individual human bidders in each auction market. 3. James (2007) shows that with experience, risk preference estimates from the buying and selling versions of the BDM procedure converge in the vicinity of risk neutrality, but nowhere near the estimates from FPSB auctions. Engel (2011) compares risk preferences measured in FPSB auctions (with human rivals) to measures using the Holt-Laury (2002) elicitation procedure, reporting much closer correspondence between the two than Isaac and James do. 4. Elbittar (2009) looks at FPSB auctions with two bidders who know the rank of their valuation. Estimating bid functions assuming constant relative risk aversion, both low- and high-value subjects bid as if they

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5. 6.

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are significantly less risk averse after information about their ranking is released. That is, information about relative rankings seems to alleviate the strategic uncertainty associated with FPSB auctions, inducing both higher- and lower-ranked subjects to bid lower relative to their valuations, which certainly seems counterintuitive for the lower-valued bidder. The risk version parameter r i is estimated form the CRRA bid function bi = (N − 1)/(N − 1 + r i )vi . There is considerable variation in the extent of bidding above the RNNE relative to the number of computerized rivals under the different treatments: more than 50% bidding above the RNNE under all three treatments with 3 and 4 computer rivals, but less than 33% with 9 computer rivals in treatments 1 and 3; 67% in treatment 3). Ockenfels and Selten (OS; 2005) report similar results from a series of FPSB auctions with two human bidders under treatment conditions 2 and 3; with experience average bids are consistently higher under treatment 2. Similar results are reported with four human bidders in Isaac and Walker (IW; 1985). In both OS and IW, there is a clear tendency for the bid ratio (bid/value) to increase more often following a lost income earning opportunity than for it to decrease following “money left on the table” in case of winning under 3. OS argue that since the impulse to decrease bids is not present in treatment 2, this accounts for the bid ratio increasing more with experience (bidders act as if they are more risk averse) than in treatment 3. They go on to attribute the greater responsiveness to lost income-earning opportunities to a social comparison process along the lines developed in Bolton and Ockenfels (2000) and Fehr and Schmidt (1999). However, the fact that responses to treatments 2 and 3 are the same with computerized as well as human rivals would seem to argue against a social comparison process. Finally note that Cason and Friedman (1997, 1999) report similar asymmetric responses to lost income-earning opportunities as opposed to leaving money on the table in two-sided SB auctions. See Kagel and Levin (1993) for a similar prediction and results in third-price SB auctions. See Engelbrecht-Wiggans (1989) for an earlier discussion of the potential effect of regret on bids in firstprice private-value auctions. Linear bid functions were estimated with no intercept. FO also report the results of a survey in which subjects were asked to rate the intensity of emotions they would feel after they got the relevant information. They find that loser’s regret is substantially more intense than the regret in the other two treatments. FO go on to show that winner’s regret has no role to play in second-price, English, and Dutch auctions, but that loser’s regret can impact Dutch auctions. They also have an interesting test for CRRA in which they report earnings back to bidders aggregated over 10 auctions, as opposed to auction by auction as is typically done. Under CRRA aggregated earnings should lead to less overbidding relative to the RNNE compared to knowing earnings following each auction. Their test provides no support for CRRA. Hayashi and Yoshimoto (2012) construct a structural model of bidder behavior in sealed-bid auctions that nests risk aversion and regret aversion. Applying the model to two sets of experimental data, they conclude that bidders exhibit weak risk aversion (close to risk neutrality) and strong regret aversion. One unanswered question that might be worth exploring is what does regret theory have to say about bids relative to the RNNE in third-price auctions (Kagel and Levin 1993) or in Cason’s (1995) emission trading auctions. For a similar exercise with respect to common value auctions, see Armantier (2002). The RNNE model provides a reasonably good fit to the data in auctions with six bidders, but risk aversion is necessary to explain bidding in auctions with three bidders. In each auction bidders got to see if they won the auction and how much they earned, with no one seeing what anyone else bid or earned. Consider the last round of a 2-round tournament with valuations from the interval [0, 10], where bidder 1 has a lead of 4 points and gets a signal of 5. Bidding 8 dominates sincere bidding as it assures winning the tournament. The difference in overbidding between buyers and sellers is significant at the 5% level in a linear regression. Subjects were told that they could lose part, or all of, their $15 participation fee in case they won the auction with the second-highest bid above their value. GWW’s results have been cited several times as demonstrating that the tendency to overbid in SPSB auctions disappears for experienced bidders. It is hard to see how this conclusion could be reached once one looks at the detailed data, or the aggregate data conditional on bidders’ eBay experience. On this score also see Dyer, Kagel, and Levin (DKL; 1989) along with Dyer and Kagel (DK; 1996). Also see Fréchette (2015) for a survey of differences in laboratory behavior between professionals and students and, more generally, across diverse subject populations (Chapter 7 in this book). ACK employ an (augmented) dual market technique with subjects bidding in each of 3 markets with the same valuations. In the first market bidders have information only about the common distribution

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from which values were drawn. In the second market precise information about one other bidder’s value is provided, and in the third market information about all other bidders’ values is provided. ACK also explore the impact of information about rivals’ values in first-price auctions where the theory makes clear predictions, which are largely satisfied, at least qualitatively. Efficiency is measured by the ratio [winner’s value]/[highest value] ∗ 100. Note, however, that the revenue reversal remains even after looking at bidding in the last 30 auctions, where learning should have stabilized. No statistical tests are reported for this. There are a couple of different ways to think about what’s going on here. The firms have merged so that the bidder with the higher private value is the firm’s value. Alternatively, there is a consortium of bidders who bid jointly and agree to allocate the item to the bidder with the highest value, along with some agreed upon device for splitting the profits. All this is in the background, because in order to simplify the experimental design, “merged” firm bids are determined by the experimenter, with profits split equally in case of a joint bid. This result is similar to results from horizontal mergers in a Cournot oligopoly (Levin, 1990). This is partly an artifact of how efficiency is typically measured when comparing efficiency between different auction structures. One solution is to normalize efficiency measures by the difference from random bidding in each case. The Amsterdam auction has been used to sell real estate in the Dutch capital for centuries. Premium auctions of this sort are regularly employed in Europe for a variety of items. Net revenues are reported for the Amsterdam auctions, defined as the winner’s payment less the premiums paid to the stage two bidders. The premium was set at 0.3 in the experiment. Hu, Offerman, and Onderstal (2011) compare the collusive properties of FPSB and English clock auctions to that of the Amsterdam SP auction. Corns and Schotter (1999), in a proof-of-principle experiment, demonstrate that proper price preference rules in favor of historically disadvantaged bidders can both increase their representation and reduce procurement costs. Ayers and Cramton (1996) report the results of what amounts to a “natural experiment” demonstrating the revenue-raising effects of price preferences in one of the Federal Government’s airwave-rights auctions. Given asymmetric valuations, with weak types bidding more aggressively than strong types, it is natural to think of auctions with resale opportunities, which has motivated a growing theoretical literature (see Hafalir and Krishna 2008; Haile 2003; Garratt and Troeger 2006). These models have started to be explored experimentally (Georganas and Kagel 2011; Lange et al. 2011; Pagnozzi and Saral 2014). In an earlier paper, Burns (1985) compared bidding in a sequential auction between wool buyers and students in which both groups were motivated “by a desire to succeed in their chosen field.” Both groups started out with declining average prices, with the students eventually converging to constant average prices. In contrast, the wool buyers continued to have declining average prices throughout the session. Burns attributed the latter to rules of thumb relevant to field settings but not the more austere conditions of her experimental markets. KO report two other treatments designed to represent the impact of agents bidding on behalf of principals, with agents penalized for failure to obtain items. NPC also have treatments with uncertain supply, where the RNNE is predicted to result in decreasing prices. For an experiment in which sellers can vary quality characteristics and compete on that dimension in addition to price, see Chen-Ritzo et al. (2005). Also see Elmaghraby et al. (2010) for a BD experiment comparing rank feedback with price feedback in BD auctions. In the English auctions with public information, there is jump bidding (a bid that is greater than the minimum bid increment). As a result, losing bidders sometimes stop short of their cost and winning bidders overshoot the second-best bid. Jump bidding tends to lower efficiency, but the two effects tend to cancel each other out with respect to buyer surplus. They also have treatment conditions where human subjects play the role of buyers, deciding whether or not to prequalify potential entrants (see WDK for details). The advantage of affiliated private values is that except for end-point effects, bidders do not know if they have a high- or low-signal value. This is valuable since in IPV auctions bidders with low valuations know they have little chance of winning the auction, which results in a number of “throwaway” bids. The affiliated private values model largely eliminates such bids except near the end points of the underlying distribution, as with affiliation bidders do not know if they have a relatively high or low value. See Turocy and Watson (2012) for indirect support for this conjecture.

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Chapter 9 40. Prices started at ν, as any other price rule would reveal information about x0 . Prices increased by smaller and smaller increments as bidders dropped out, with brief pauses following each dropout. 41. The intuition behind this is roughly as follows: Given symmetry, the low-signal holder knows that those remaining in the auction have higher signal values so that his or her estimate of x0 is higher than x L . But the low-signal holder can’t profit from this additional information since not dropping at x L pushes the price up, so that winning at a higher price, when others drop at equilibrium prices, assures the low bidder negative expected profit. 42. Common value auctions involve pure surplus transfers so that revenue differences are calculated as: [π E − π F ] where π E and π F correspond to profits in English and FPSB auctions, respectively. This effectively normalizes for sampling variability in xo by subtracting it from the price. 43. One-tailed t-tests are conducted for predicted revenue increases since the symmetric RNNE makes unambiguous predictions regarding revenue. Two-tailed t-tests are used for determining statistical significance of actual revenue changes since the presence of a WC promotes lower revenue in English auctions. 44. There is no analytic solution to the system of differential equations that characterizes the Nash equilibrium in Kagel and Levin (1999). However, see Campbell and Levin (2006) for a model that solves for the Nash equilibrium analytically, where the introduction of an insider can raise revenue as well. 45. See Rose and Kagel (2008) for similar results under the Kagel and Levin (1986) design, where bidders’ signals are drawn uniformly from the interval [x0 − ε, x0 + ε] using experienced bidders who had overcome the worst effects of the WC in FPSB auctions. Also, see Georganas and Nagel (2011) who explore the predictions of the closely related “toehold” model using an English clock auction, reporting similar results. 46. As CI note, their model cannot explain the winner’s curse in SP CVAs or the persistent overbidding in FP private value auctions. Nevertheless, this paper is important because it shows a totally unanticipated result for FP CVAs. The failure to explain overbidding in SP CVAs can be rationalized by the fact that subjects simply do not understand SP auctions very well, whether private or common value. 47. Also see Tor and Bazerman (2003), who argue that the WC in the takeover game results from buyers ignoring sellers’ cognitive processes. 48. There is little change over time in the frequency of 0 bids or bids of 20 in the 0–99 and 20–119 treatments. Further, it does not appear that many subjects consistently bid 0 or 20 in these treatments. 49. In their formulation the common value component depends on the average of bidders’ common value signals. 50. Bankrupt bidders from inexperienced subject sessions were not invited back for experienced sessions. 51. Similar gender effects are identified by Charness and Levin (2009) in the closely related takeover game. 52. To be sure, there are alternative explanations for the field data (see Kagel and Levin 1986), but the WC is a much more straightforward explanation than the alternatives offered. 53. Subjects were not provided with any starting capital balances or participation fees to cover potential losses. Rather, a second experiment, not announced until the first experiment was completed, was used to ensure that subjects went home with positive earnings. Given the potential impact of limited liability for losses on bids (Kagel and Levin, 1991), failure to announce in advance how potential losses would be covered is problematic at best. 54. Shaving of bids relative to signal values averaged 40% (82%) for nondealers versus 93% (88%) for dealers with ε = $6 ($12). 55. For a good primer from the psychology literature on learning generalizability, see Salomon and Perkins (1989). Or, as the Noble laureate Richard Feynman (2005, 39) put it, “I don’t know what’s the matter with people: they don’t learn by understanding; they learn by some other way—by rote, or something. Their knowledge is so fragile.” 56. For example, auctions for book-publication rights (Dessauer 1981), professional baseball’s free-agency market (Cassing and Douglas 1980; Blecherman and Camerer 1998), corporate takeover battles (Roll 1986), and real estate auctions (Ashenfelter and Genesove 1992). 57. With bidders having the same value for 2 units, we refer to the higher bid as the bid on unit 1 and the lower bid to the bid on unit 2. 58. For example, assume a support for values of between [0, 100] with the values for both units for the human bidder, vh , of 90. Suppose that h has no formal understanding of the optimal bidding strategy and decides to remain active as long as p ≤ vh . Suppose that v2 drops out at 50. Now h has two options, drop at 50 and earn an instant profit of 40 or remain active in an effort to win both units. In the latter case there are two events to consider: (1) the highest computer rival (v1 ) drops prior to p = vh , in which case h’s expected profit is 40 (as 70 is the expected drop price for v1 ), or (2) v1 ≥ vh ≥ 90, in which case h’s expected profit is zero. Thus, dropping at p = v2 dominates waiting and trying to win 2 units. This is not to say that

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60.

61.

62.

63. 64.

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these calculations are trivial, but they are far more transparent than the ex ante calculations underlying the optimal bidding strategy in the SB auctions. Further, if h remains active once p > v2 , it should be increasingly transparent that she is competing against herself, which should lead to dropping out before the price is equal to vh , which might help promote learning over time. Results are pooled over auctions with 3 and 5 computer rivals. All data are for the last 12 auctions in a session. Subjects were never told that the computers were following a dominant strategy, just that they would drop out at their randomly drawn values. For dropouts above value, diamonds represent harmless over bids and triangles represent potentially harmful over-bids. Harmless over-bids involve dropping out prior to the third highest computer dropping. Potentially harmful over-bids involve dropping out after the third highest computer dropped, so the bidder would have lost money had one of the computerized bidders dropped before they did. Clinching works as follows: With 2 objects for sale, suppose at a given price, p, the human bidder (h) still demands 2 units, but the aggregate demand of all other bidders has dropped from 2 to 1. Then, in the language of team sports, bidder h has clinched a unit no matter how the auction proceeds. As such, at that moment, h is awarded 1 unit at the clinching price, p. The auction continues with the supply reduced from 2 to 1 and h’s demand reduced to 1 unit. This process repeats itself until all units are allocated. In this way the auction sequentially implements the Vickrey rule that each bidder pays the amount of the kth-highest rejected bid, other than his or her own, for the kth unit won. Here too triangles represent harmless over-bids, with diamonds representing potentially harmful over-bids. With two items both having the same value, there are two equilibria: one with value bidding on the first unit and demand reduction on the second-unit, and an equilibrium with value bidding on both units (Ausubel and Cramton, 1996). EG also report on discriminatory auctions with this design. One of their most interesting results in this case involves submitting different bids on the two items (bid spreading), where bidders should submit equal bids for both items. In this case, 58% of unit 2 bids are below the RNNE without any discernable time trend, which is inconsistent with risk aversion (Grimm and Englemann 2005). Kagel and Levin (2005) also report bid spreading where it should not occur in multiunit demand auctions with synergies. This equilibrium is distribution free and has no regret, so bidders have limited incentive to deviate to the equilibria discussed earlier. While the SB Vickrey auction only requires rationality on the part of bidders, iterated deletion of dominated strategies adds the requirement of common knowledge of rationality, a far from trivial addition, so that from a mechanism design standpoint the SB Vickrey auction is more robust and more desirable. A closely related experiment that deserves mention here is Kagel et al. (2007), who compare the Ausubel auction to the strategically equivalent survivor auction, in which the Ausubel auction is essentially implemented through a series of SB auctions. In spite of the similarity in structure and information feedback between the two auction formats, the Ausubel auction achieves significantly higher levels of sincere bidding and efficiency than the survivor auction to begin with, so that only with experience does the survivor auction come close to the performance of the Ausubel auction. Manelli, Sefton and Wilner (2006) find little difference between the Ausubel auction with dropout information provided and a SB Vickrey auction, including rather limited bidding above value on unit 1 bids in the SB auctions. The best explanation we have to offer for this given the strong evidence for the differences reported in KL and KKL and in single unit auctions is sampling variability, or subject pool effects. Isaac and James (2000b) and Morgan (2002) study a SB VCG auction with 2 items and synergies, involving only 3 possible packages to bid on. Given the limited number of items in question, subjects bid on almost all possible packages in both studies. There is no threshold problem in UP auctions for single-unit-demand bidders since under the UP rule, no small bidder can obtain a unit at a lower price than the other small bidder. CL require the global bidder to place the same bid on both items in the absence of package bids. See Kagel and Levin (2005) for one additional experiment dealing with these issues. Pitchik and Schotter (1988) have an earlier paper on budget-constrained bidders in sequential auctions. Their subjects have full information about each other’s values and budget constraints, with a focus on sorting out between different equilibrium refinements. BR refer to two empirical studies as providing support for their design: Jofre-Bonet and Pesendorfer (2000, 2003) found that firms that did not win a highway-paving contract earlier in a sequence of auctions were more likely to enter a subsequent auction than firms that had already won a contract. De Silva, Dunne, and Kosmopoulou (2002) found that in auctions held by the Oklahoma Department of Transportation, firms that lost in morning auctions bid more aggressively in the afternoon auctions compared to firms

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76.

77. 78.

79. 80. 81. 82. 83. 84.

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that had won in the morning. Also see DK, who report that the overhead rates attached to bids by general contractors are positively related to the number of jobs already won. See Hu, Offerman, and Onderstal (2009) for the sole single-unit auction study we have identified since the 1995 survey. See Menkhaus, Phillips, and Coatney (2003) for a related experiment. See BL for a full characterization of the Nash equilibrium, which also holds for strong synergies between items and when two or more bidders have higher values for the same unit. Cramton and Schwartz (2002) provide evidence for BL-type collusion in the FCC’s auctions for spectrum licenses. EG (Section 3.1) report attempts at collusion in their SAA auctions with repeated matching. On this last point KLM report two clear instances of such a collusive outcome in CCA auctions with random rematching in each auction. The facilitating practices in KLM consisted of announcing provisional winners and determining provisional allocations randomly in case of tied bids (as opposed to maximizing the number of players with no items). Interestingly, in theory at least, BL-style tacit collusion can be achieved in the case of large complements but not with moderate complements. Brown, Sullivan, and Plott (2009) show both theoretically and in an experiment that switching to a simultaneous descending-price auction in which all bids are final serves to break up the collusive Nash equilibrium within the incubator structure. Demand was simulated in the product market with price-taking consumers. There is considerably more to this rich experiment than reported on here, including a monopoly treatment in which monopoly rights are bid for or simply awarded. On this point also see Sherstyuk (2002). See http://www.aaauctionservice.com/glossery_files/glossery.htm. There were no restrictions on the probabilities, so that it was possible to have fewer than 2 bidders whose preferred item was A or B. Their loss-averse specification uses the utility function and parameter values reported in Tversky and Kahneman (1992). SI note that there is little difference between risk-neutral and risk-averse bidding given their parameter values. Their SAA follows the format employed in the Federal Trade Commission spectrum auctions, with a countdown clock that resets every time a new bid is submitted. The auction ends when no new bids are submitted for any items, with winning bidders paying what they bid. Bajari and Hortacsu (2004) and Ockenfels et al. (2006) provide surveys of theoretical, empirical, and experimental work on Internet auctions. Different Internet auction platforms adopt different BIN options. In eBay bidders have a chance to get the item at a fixed price before any bids are placed. In Yahoo the BIN can be exercised after bidding starts. Also see Ivanova-Stenzel and Kröger (2008), who investigate BIN auctions in which a seller (played by one of the participants) offers a BIN to one of the two potential buyers. Endoginizing entry decisions extends to accounting for bidders’ preferences over auction institutions (Mathews 1987; McAfee and McMillan 1987). Most of the research on this topic is in the context of a private value auction. This approach also allows for symmetric risk-averse bidders. For example if u(x) = x ρ , where ρ is the CRRA parameter than in equilibrium q ∗ = Q ∗ (c, N|ρ). There is a large, closely related, earlier experimental literature on coordination games (see Ochs 1995: Rapoport et al. 1998; and references therein). The key difference between SL’s experiment and these earlier ones is linking the payoff structure to what would have been earned in the RNNE of a well-defined auction market. To assure competitiveness, 1 bidder was assigned to each format without any choice so that each of the remaining 4 bidders could not enter and find himself or herself the only bidder in that market. See ISS for a number of other important details regarding the innovative procedures employed. The experiment was inspired by developments in spectrum auctions in both the United States and Germany. Hu et al. (2013) report results from a single-item experiment in which a potential entrant, if he or she wins the auction, imposes a negative externality on two incumbents. Entry rates are significantly higher in the FPSB auction compared to the clock auction, consistent with the model’s prediction. Three different FP formats were employed—all licenses sold at the same time, sequential sale of licenses, and a simultaneous descending (Dutch auction) format. Entry rates were lower, with the probability of winning essentially the same, under the sequential FP format compared to the SAA.

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Hendricks, K., R. H. Porter, and C. A. Wilson. 1994. Auctions for Oil and Gas Leases with an Informed Bidder and a Random Reservation Price. Econometrica 62: 1415–44. Holt, C., and S. Laury. 2002. Risk Aversion and Incentive Effects. American Economic Review 92: 1644–55. Holt, C. A. Jr., and R. Sherman. 1994. The Loser’s Curse and Bidder’s Bias. American Economic Review 84: 642–52. Hu, A., Offerman, T. and S. Onderstal. 2011. Fighting Collusion in Auctions: An Experiental Investigation. International Journal of Industrial Organization 29(1): 84–96. Hu, Y., J. H., Kagel, X. Xu, and L. Ye. 2013. Theoretical and Experimental Analysis of Auctions with Negative Externalities. Games and Economic Behavior 82: 269–91. Isaac, R. M., and D. James. 2000a. Just Who Are You Calling Risk Averse? Journal of Risk and Uncertainty 20: 177–87. ———. 2000b. Robustness of the Incentive Compatible Combinatorial Auction. Experimental Economics 3: 31–53. Isaac, R. M., and J. M. Walker. 1985. Information and Conspiracy in Sealed Bid Auctions. Journal of Economic Behavior and Organization 6: 139–59. Ivanov, A., D. Levin, and M. Niederle. 2010. Can Relaxation of Beliefs Rationalize the Winner’s Curse? An Experimental Study. Econometrica 78: 1435–52. Ivanova-Stenzal, R., and T. C. Salmon. 2008. Revenue Equivalence Revisited. Games and Economic Behavior 64: 171–92. Ivanova-Stenzel, Radosveta, and Sabine Kröger. 2008. Price Formation in a Sequential Selling Mechanism. Journal of Economic Behavior & Organization 67: 832–43. James, D. 2007. Stability of Risk Preference Parameter Estimates within the Becker-DeGrootMarschak Procedure. Experimental Economics 10: 123–42. Jap, S. D. 2002. Online Reverse Auctions: Issues, Themes and Prospects for the Future. Journal of Academic Marketing Science 30: 506–25. Jofre-Bonet, M., and M. Pesendorfer, 2000. Bidding Behavior in a Repeated Procurement Auction. European Economic Review, Revised 44: 1006–20. ———. 2003. Estimation of a Dynamic Auction Game. Econometrica 71: 1443–89. Johnson-Laird, P. N. 1999. Deductive Reasoning. Annual Review of Psychology 50: 109–35. Kagel, J. H. 1995. Auctions: A Survey of Experimental Research. In,Alvin E. Roth and John H. Kagel, eds., The Handbook of Experimental Economics, Vol. 1. Princeton, NJ: Princeton University Press. Kagel, J. H., R. M. Harstad, and D. Levin. 1987. Information Impact and Allocation Rules in Auctions with Affiliated Private Values: A Laboratory Study. Econometrica 55: 1275–1304. Kagel, J. H., S. Kinross, and D. Levin. 2001. Comparing Efficient Multi-Object Auction Institutions. Working paper, Ohio State University. Kagel, J. H., and D. Levin. 1986. The Winner’s Curse and Public Information in Common Value Auctions. American Economic Review 76: 894–920. ———. 1991. The Winner’s Curse and Public Information in Common Value Auctions: Reply. American Economic Review 81: 362–69. ———. 1993. Independent Private Value Auctions: Bidder Behavior in First-, Second- and ThirdPrice Auctions with Varying Numbers of Bidders. Economic Journal 103: 868–79. ———. 1999. Common Value Auctions with Insider Information. Econometrica 67: 1219–38. ———. 2001. Behavior in Multi-Unit Demand Auctions: Experiments with Uniform Price and Dynamic Vickery Auctions. Econometrica 69: 413–54. ———. 2002. Bidding in Common Value Auctions: A Survey of Experimental Research. In Common Value Auctions and the Winner’s Curse. Princeton, NJ: Princeton University Press. ———. 2005. Multi-Unit Demand Auctions with Synergies: Behavior in Sealed- Bid versus Ascending-Bid Uniform-Price Auctions. Games and Economic Behavior 53: 170–207. ———. 2009. Implementing Efficient Multi-Object Auction Institutions: An Experimental Study of the Performance of Boundedly Rational Agents. Games and Economic Behavior 66: 221–37.

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Chapter 9 Kagel, J. H., Y. Lien, and P. Milgrom. 2010. Ascending Prices and Package Bidding: An Experimental Analysis. American Economic Journal: Microeconomics 2: 160–85. ———. 2014. Ascending Prices and Package Bidding: Further Experimental Analysis. Games and Economic Behavior 85: 210–31. Kagel, J. H., S. Pevnitskaya, and L. Ye. 2007. Survival Auctions. Economic Theory 33: 103–19. ———. 2008. Indicative Bidding: An Experimental Analysis. Games and Economic Behavior 62: 697–721. Kagel, J. H., and J. F. Richard. 2001. Super-Experienced Bidders in First-Price Common Value Auctions: Rules of Thumb, Nash Equilibrium Bidding and the Winner’s Curse. Review of Economics and Statistics 83: 408–19. Katok, E., and A. E. Roth. 2004. Auctions of Homogeneous Goods with Increasing Returns: Experimental Comparison of Alternative “Dutch” Auctions. Management Science 50: 1044–63. Keser, C., and M. Olson. 1996. Experimental Examination of the Declining-Price Anomaly. In. V. Ginsburg and P-M Menger, eds., Economics of the Arts: Selected Essays. Amsterdam: Elsevier. Klemperer, P. 1998. Auctions with Almost Common Values: The “Wallet Game” and its Applications. European Economic Review 42: 757–69. ———. 2002. How (Not) to Run Auctions: The European 3G Telecom Auctions. European Economic Review 46: 829–45. Krishna, V. 2002. Auction Theory. Academic Press. Kwasnica, A. M., and K. Sherstyuk. 2007. Collusion and Equilibrium Selection in Auctions. Economic Journal 117: 120–45. Lange, A., J. A. List, and M. K. Price. 2011 Auctions with Resale When Private Values Are Uncertain: Theory and Empirical Evidence. International Journal of Industrial Organization 29: 54–64. Leufkens, K., R. Peeters, and M. Vorsatz. 2006. Sequential Auctions with Synergies: An Experimental Study. METEOR Research Memorandum 06/040, Maastricht University. Levin, D. 1990. Horizontal Mergers: The 50 Percent Benchmark. American Economic Review 80: 1238–45. ———. 2005. Demand Reduction in Multi-Unit Auctions: Evidence from a Sportscard Field Experiment: A Comment. American Economic Review 95: 467–71. Levin, D., and J. H. Kagel. 2005. Almost Common-Value Auctions Revisited. European Economic Review 49: 1125–36. Levin, D., J. H. Kagel, and J. F. Richard. 1996. Revenue Effects and Information Processing in English Common Value Auctions. American Economic Review 86: 442–60. Levin, D., and J. Smith. 1994. Equilibrium in Auctions with Entry. American Economic Review 84: 585–99. Li, J., and C. R. Plott. 2009. Tacit Collusion in Auctions and Conditions for Its Facilitation and Prevention: Equilibrium Selection in Laboratory Experimental Markets. Economic Inquiry 47(3): 425–48. Lind, B., and C. R. Plott. 1991. The Winner’s Curse: Experiments with Buyers and with Sellers. American Economic Review 81: 335–46. List, J. A., and D. Lucking-Reiley. 2000. Demand Reduction in Multi-Unit Auctions: Evidence from a Sportscard Field Experiment. American Economic Review 90: 961–72. Loomes, G., and R. Sugden. 1982. Regret Theory: An Alternative Theory of Rational Choice under Uncertainty. Economic Journal 92: 805–24. Lucking-Reiley, D. 1999. Using Field Experiments to Test Equivalence between Auction Formats: Magic on the Internet. American Economic Review 89: 1063–80. Manelli, A. M., M. Sefton, and B. S. Wilner. 2006. Multi-Unit Auctions: A Comparison of Static and Dynamic Mechanisms. Journal of Economic Behavior and Organization 61: 304–23. Maskin, E., and J. Riley. 2000. Asymmetric Auctions. Review of Economic Studies 67: 413–38. Matthews, S. 1987. Comparing Auctions for Risk Averse Buyers: A Buyer’s Point of View. Econometrica 55(3): 633–46.

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Mathews, T. 2003. The Impact of Discounting on an Auction with a Buy-Out Option: A Theoretical Analysis Motivated by eBay’s Buy-It-Now Feature. Journal of Economics (Zietschrift für Nationalökonomie) 81: 25–52. McAfee, R. P., and J. McMillan. 1987. Auctions with Entry. Economic Letters 23: 343–47. McAfee, R. P., and D. Vincent. 1993. The Declining Price Anomaly. Journal Economic Theory 60: 191–212. Mellers, B. A., and A. D. J. Cooke. 1996. The Role of Task and Context in Preference Measurement. Psychological Science 7: 76–82. Menezes, F. M., and P. K. Monteiro. 1998. Simultaneous Pooled Auctions. Journal of Real Estate Finance and Economics 17: 219–32. Menkhaus, D. J., O. R. Phillips, and K. T. Coatney. 2003. Shared Agents and Competition in Laboratory English Auctions. American Journal of Agricultural Economics 85: 829–39. Morgan, J. 2002. Combinatorial Auctions in the Information Age: An Experimental Study. Advances in Applied Microeconomics 11: 191–207. Myerson, E. 1981. Optimal Auction Design. Mathematics of Operations Research 6: 58–73. Neugebauer, T., and P. Pezanis-Christou. 2007. Bidding Behavior at Sequential First-Price Auctions with(out) Supply Uncertainty: A Laboratory Analysis. Journal of Economic Behavior & Organization 63: 55–72. Neugebauer, T., and R. Selten. 2006. Individual Behavior and First-Price Auctions: The Importance of Information Feedback in Computerized Experimental Markets. Games and Economic Behavior 54: 183–204. Niederle, M., and L. Vesterlund. 2007. Do Women Shy Away from Competition? Quarterly Journal of Economics 122: 1067–1101. Ochs, J. 1995. Coordination Problems. In J. H. Kagel and A. E. Roth, eds., Handbook of Experimental Economics, Vol. 1. Princeton, NJ: Princeton University Press. 195–251. Ockenfels, A., D. H. Reiley, and A. Sadrich. 2006. Online Auctions. In T. Hendershott. ed. Handbook of Information Systems. Amsterdam, Netherlands: Elsevier, 571–628. Ockenfels, A., and R. Selten. 2005. Impulse Balance Equilibrium and Feedback in First Price Auctions. Games and Economic Behavior 51: 155–70. Offerman, T. and J. Potters. 2006. Does Auctioning of Entry Licenses Induce Collusion? An Experimental Study. Review of Economic Studies 73: 769–91. Pagnozzi, M., and K. J. Saral. 2014. Multi-Object Auctions with Resale: An Experimental Analysis. Working paper, Università di Napoli Frederico II. Palfrey, T., and S. Pevnitskaya. 2008. Endogenous Entry and Self-Selection in Private Value Auctions: An Experimental Study. Journal of Economic Behavior and Organization 66: 731–47. Pezanis-Christou, P. 2002. On the Impact of Low-Balling: Experimental Results in Asymmetric Auctions. International Journal of Game Theory 31: 69–89. Phillips, O. R., and D. J. Menkhaus. 2009. Maintaining Tacit Collusion in Repeated Ascending Auctions. Journal of law and Economics 52: 91–110. Phillips, O. R., D. J. Menkhaus, and K. T. Coatney. 2003. Collusive Practices in Repeated English Auctions: Experimental Evidence on Bidding Rings. American Economic Review 93: 965–79. Pitchik C., and A. Schotter. 1988. Perfect Equilibria in Budget-Constrained Sequential Auctions: An Experimental Study. Rand Journal of Economics 19: 363–88. Porter, D., and R. Vragov. 2006. An Experimental Examination of Demand Reduction in MultiUnit Versions of the Uniform-Price, Vickery, and English Auctions. Managerial and Decision Economics 27: 445–58. Rabin, M. 2000. Risk Aversion and Expected Utility Theory. Econometrica 68: 1281–92. Rapoport, A., D. Seale, I. Erev, and J. Sundali. 1998. Equilibrium Play in Large Group Market Entry Games. Management Science 44: 119–41. Reynolds, S. S., and J. Wooders. 2009. Auctions with a Buy Price. Economic Theory 38: 9–39.

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Chapter 9 Riley, J. G., and W. F. Samuelson. 1981. Optimal Auctions. American Economic Review 71: 381–92. Robert, J., and C. Montmarquette. 1999. Sequential Auctions with Multi-Unit Demand: Theory, Experiments and Simulations. CIRANO working paper, 99s-46. Roll R. 1986. The Hubris Hypothesis of Corporate Takeovers. Journal of Business 59: 197–216. Rose, S. L., and J. H. Kagel. 2008. Bidding in Almost Common Value Auctions: An Experiment. Journal of Economic Management Strategy 17: 1041–58. Rose, S. L., and D. Levin. 2008. An Experimental Investigation of the Explosive Effect in Almost Common Value Auctions. Journal of Economic Behavior and Organization 67: 927–46. Roth, A. E., and A. Ockenfels. 2002. Last-Minute Bidding and the Rules for Ending SecondPrice Auctions: Evidence from eBay and Amazon Auctions on the Internet.American Economic Review 92: 1093–1103. Sade, O., C. Schnitzlein, and J. F. Zender. 2006. Competition and Cooperation in Divisible Good Auctions: An Experimental Examination. Review of Financial Studies 19: 195–235. Salmon, T. C., and M. Iachini. 2007. Continuous Ascending vs. Pooled Multiple Unit Auctions. Games and Economic Behavior 61: 67–85. Salmon, T. C., and B. J. Wilson. 2008. Second Chance Offers versus Sequential Auctions: Theory and Behavior. Economic Theory 34: 47–67. Salomon, G., and D. N. Perkins. 1989. Rocky Roads to Transfer: Rethinking Mechanisms of a Neglected Phenomenon. Education Psychologist 24: 113–42. Samuelson, W. F. and M. H. Bazerman. 1985. The Winner’s Curse in Bilateral Negotiations, In V. L. Smith, ed., Research in Experimental Economics, 3. Greenwich, CT: JAI Press. Scheffel, Tobias, Georg Ziegler, and Martin Bichler. 2012. On the Impact of Package Selection in Combinatorial Auctions: An Experimental Study in the Context of Spectrum Design. Experimental Economics 15(4): 667–92. Shahriar, Q., and J. Wooders. 2011. An Experimental Study of Auctions with a Buy Price under Private and Common Values. Games and Economic Behavior 72(2): 558–73. Sherstyuk, K. 2002. Collusion in Private Value Ascending Price Auctions. Journal of Economic Behavior and Organization 48(2): 177–95. Shogren, J. F., G. M. Parkhurst, and C. McIntosh. 2006. Second-Price Auction Tournament. Economics Letters 92: 99–107. Smith, J. 1982. Equilibrium Patterns of Bidding in OCS Lease Sales. Economic Inquiry 20: 180–90. Smith, J., and D. Levin. 2001. Entry Coordination in Auctions and Social Welfare: An Experimental Investigation. International Journal of Game Theory 30: 321–50. Smith, J. L. 1984. Further Results on Equilibrium Patterns of Bidding in OCS Lease Sales. Economic Inquiry 22: 142–146. Tor, A., and M. H. Bazerman. 2003. Focusing Failures in Competitive Environments: Explaining Decision Errors in the Monty Hall Game, the Acquiring a Company Game, and Multiparty Ultimatums. Journal of Behavioral Decision Making 16: 353–74. Turocy, T. L., and E. Watson. 2012. Reservation Values and Regret in Laboratory First-Price Auctions: Context and Bidding Behavior. Southern Economic Journal 78(4): 1163–80. Turocy, T. L., E. Watson, and R. C. Battalio. 2007. Framing the First-Price Auction. Experimental Economics 10: 37–52. Tversky, A., and D. Kahneman. 1992. Advances in Prospect Theory: Cumulative Representation of Uncertainty. Journal of Risk and Unvertainty 5: 297–323. Vickrey, W. 1961. Counterspeculation, Auctions, and Competitive Sealed Tenders. Journal of Finance 16: 8–37. Walker, J. M., V. L. Smith, and J. C. Cox. 1987. Bidding Behavior in First-Price Sealed-Bid Auctions: Use of Computerized Nash Competitors. Economic Letters 23: 239–44. Whinston, M. D. 2006. Lectures on Antitrust Economics. Cambridge, MA: MIT Press. Wilson, B. R. 1967. Insider Competitive Bidding with Asymmetric Information. Management Science 13: 816–20.

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10 Learning and the Economics of Small Decisions Ido Erev and Ernan Haruvy

INTRODUCTION Mainstream analysis of economic behavior assumes that economic incentives can shape behavior even when individual agents have limited understanding of the environment (see related arguments in Nash1 1950; Smith2 1962). The shaping process in these cases is indirect: The economic incentives determine the agents’ experience, and this experience in turn drives future behavior. Consider, for example, an agent that has to decide whether to cross the road at a particular location and time. The agent (say a chicken) is not likely to understand the exact incentive structure and compute the implied equilibria. Rather, the agent is likely to rely on experience with similar situations. The economic environment shapes this decision because it determines the relevant experience. The current chapter reviews experimental studies that examine this shaping process. In order to clarify the relationship of the research reviewed here to classical research in behavioral and experimental economics it is constructive to consider the distinction between “decisions from description” and “decisions from experience” (Hertwig et al. 2004) exemplified in Figure 10.1. Classical studies in behavioral economics tend to focus on decisions from description: They examine how people decide when they can rely on a complete description of the incentive structure. In contrast, the research reviewed here focuses on decisions from experience. In a pure decision from an experience task (like the one demonstrated in Figure 10.1), the decision makers do not receive a prior description of the incentive structure. Rather, they have to rely on past experience, and gain relevant experience in the course of the experiment. The two lines of decision research have similar goals but take very different routes towards achieving these goals. As a result, the two routes often identify and focus on different behavioral regularities. The main difference between the two routes is reflected by the relationship of the two lines of research to rational economic theory. The classical studies of decisions from description were designed to test the rationality assumption. The most influential papers in that research stream (e.g., Allais 1953; Kahneman and Tversky 1979; Fehr and Schmidt 1999; Bolton and Ockenfels 2000) present interesting

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Decisions from description: the decisions under risk paradigm Please select one of the following prospects: Win 4,000 with probability 0.80 0 otherwise (probability 0.20) Win 3,000 with certainty

Decisions from experience: the clicking paradigm The current experiment includes many trials. Your task, in each trial, is to click on one of the two keys presented on the screen. Each click will be followed by the presentation of the keys’ payoffs. Your payoff for the trial is the payoff of the selected key.

Figure 10.1: Typical instruction screen in studies of decisions from description (using the “decisions under risk paradigm”) and studies of decisions from experience (using the “clicking paradigm”).

deviations from rational choice and elegant refinements of the rational models that capture these deviations. Gigerenzer and Selten (2001) broadly refer to this line of research as the “subjective expected utility repair program.” In contrast, the studies of decisions from experience focus on situations for which rational decision theory does not have clear predictions. When decision makers rely on past experience, almost any behavior could be justified as rational given their experience and the beliefs this fosters. Thus, the study of decisions from experience is not designed to test or refine rational decisions theory; rather, it is intended to expand the set of situations that can be addressed with economic models that provide clear and useful predictions. The significance of the difference between the behavioral regularities discovered in the two lines of decision research is demonstrated by the effect of rare (low-probability) events. Experimental studies reveal that people exhibit oversensitivity to rare events in decisions from description (Kahnemna and Tversky 1979) and the opposite bias when they rely on experience (see Barron and Erev (2003) and Section 1.1.3). This “experience-description gap” suggests that the common efforts to use models that were calibrated to capture decisions from description in order to address decisions from experience can lead to mismatched conclusions. Many natural decision problems fall in between decisions from description and decisions from experience. For example, in 2003 when the president of the United States, George W. Bush, had to decide whether or not to engage militarily in Iraq, he could rely on a description of the incentive structure, prepared by his consultants, but he could also rely on historical experiences in similar situations. And it is possible that these experiences could suggest that the description can be biased.

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The importance of past experience is particularly clear in the context of small decisions. Small-decision problems are defined here as situations in which the performance of a task requires decisions, and the expected consequences of each decision are relatively small. Many natural activities involve small decisions. For example, the road-crossing task, described earlier, implies several small decisions. The agent can choose whether to start crossing in several points in time and can then choose to change his or her mind. We believe that small decisions can be of large economic importance. In many cases, small decisions can be highly consequential in the aggregate, and they can also be consequential in some rare specific cases. For example, small driving-related decisions lead to traffic jams, costly accidents, injuries, and even fatalities. Moreover, in many cases small decisions shape subsequent big decisions. For instance, the small decisions between doing homework or watching TV as a child can affect the available alternatives in the big decisions among different career paths. Similarly, the big decision between different investment portfolios is made only if the agent has made the small decision to spend time (at a particular point in time) on evaluating his or her investments.3 Economics, psychology, and the clicking paradigm. Most of the studies of learning and decisions from experience were conducted by psychologists and were not designed to evaluate the effect of the quantitative features of the incentive structure; they typically used nonmonetary reinforcements like food, electric shocks, unpleasant noises, and verbal recognition. In order to clarify the economic implications of these studies, we try to replicate the main results using the clicking paradigm presented in Figure 10.1. As demonstrated in Figure 10.1, the clicking paradigm focuses on the effect of experiencing monetary payoffs. The subjects do not receive prior description of the incentive structure and have to base their decisions on the feedback (observed monetary outcomes) of previous decisions. To facilitate evaluation of the effect of this experience, each experiment includes many trials. In order to illustrate the relationship of the current replications to the original demonstrations of the classical phenomena, we start the discussion of the key phenomena with a description of the original studies. Yet, we pay greater attention to the clicking paradigm. Another advantage of the clicking paradigm replications involves the standardization of the experimental conditions (Hertwig and Ortmann 2002). For example, it allows the use of the same instructions, same experimental design, and same subject population in the replications of the distinct regularities.4 Since we focus on phenomena that were already documented in a wide set of conditions with a wide set of subject populations (including very different animals), the focused standardization should not impair external validity. The standardization is expected to clarify the role of the key factor—the effect of experiencing the incentive structure—and facilitate the development of models that capture this effect. Three cognitive factors and the organization of the current review. Decisions from experience are likely to be affected by three classes of cognitive factors (see Erev and Roth 1999). The first factor involves the cognitive strategies considered by the agents, that is, the strategies from which the agents learn. The cognitive strategies include the possible actions (stage game strategies, “Select the left Key” or “Select the right key” in the basic clicking paradigm), but can also include other strategies like “Try to reciprocate” (see Section 4.3) or “Select best reply to the instructions” (see Section 1.1.9). The second factor involves the exploration policy—that is, the trade-off between collecting information and using the available information in order to get the

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best outcomes (see March 1991). The third factor is the choice rule: the evaluation of past experiences that determines which strategy is preferred. We believe that all three factors are important, but we also think that better understanding of the choice rule is likely to be most useful. Our belief is based on the observation that the cognitive strategies and the exploration policy tend to be situation specific. Small changes in the environment can change the strategies available and considered by the agents and can change the value of exploration. In contrast, it is possible that the choice rule reflects more robust properties of the underlying cognitive processes that are likely to be stable over situations and maybe also over species. This belief led us to start the current review with a focus on phenomena that can be replicated even when the effect of the first two factors is minimized. Specifically, we start with a focus on situations in which (1) it is reasonable to assume that the strategies considered by the agents can be approximated by the possible actions, and (2) exploration does not add information. The most important part of the current review is Section 1.1, which presents six robust behavioral phenomena that emerge in this setting and a simple model that summarizes them. We consider situations in which exploration is important in Section 1.2 and delay the discussion of situations in which more sophisticated strategies are likely to be important to Sections 2, 3, and 4. Section 2 reviews studies of learning in dynamic environments, and Section 3 reviews studies of learning among of large number of alternatives. The results highlight interactions between the basic properties of learning, summarized in Section 1, and other factors that can be abstracted as “cognitive strategies” that are implied by the task. Section 4 reviews studies that examine the effect of social interactions on learning. The first part of this section highlights the generality of the basic properties of learning reviewed in first sections. There are many situations in which social behavior can be accurately predicted based on simple models that were designed to capture behavior in individual choice tasks. Yet there are also interesting exceptions to this generality. The main exceptions can be summarized with the assertion that in certain settings prior information changes the strategies that are considered in the learning process. The chapter concludes with a discussion of the practical implications of experimental learning research. The discussion focuses on the economics of small decisions.

1 THE BASIC PROPERTIES OF DECISIONS FROM EXPERIENCE The current section reviews the learning phenomena that we consider to be most basic in the sense that they can be reliably replicated in the most basic versions of the clicking paradigm. 1.1 Six Basic Regularities and a Model Recall that the current review is based on the distinction between three cognitive factors that drive decisions from experience: the cognitive strategies, the exploration policy, and the choice rule. The present subsection tries to clarify the basic properties of the choice rule. In order to achieve this goal, it focuses on phenomena that can be replicated even when the role of sophisticated cognitive strategies and of the exploration policy is minimized. This “minimization” is achieved by using the 2-alternative clicking paradigm with complete feedback (cf. Figure 10.1) and a static payoff rule. After each choice in the clicking experiments considered here, the agents receive feedback concerning their obtained payoff (the payoff from the key selected), and the forgone

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payoff (the payoff that could have been obtained had the second key been selected). The payoff of each key is drawn from a payoff distribution associated with that key. For example, if the key is associated with payoff distribution “11 with probability .5, −9 otherwise”, the payoff will be 11 in 50% of the trials and −9 in the other 50%. The fact that the payoff rule is static implies that the distributions do not change during the experiment, and the agents can maximize expected return by selecting the option that has led to higher average payoff in the previous trials. Our review uncovers six robust behavioral regularities that emerge in this setting. All six regularities imply deviations from maximization of expected return. Yet we believe that they do not imply deviations from “ecologically reasonable” behavior. In order to clarify this assertion, we conclude the presentation of each behavioral regularity with an “ecological justification.” Section 1.1.7 presents a model that quantifies these justifications, and the subsequent sections clarify the model’s relationship to other models and its predictive value. 1.1.1 THE LAW OF EFFECT Thorndike (1898) studied how cats learn to escape from puzzle boxes. The experiments included several trials: Each trial started with the placement of a cat in a puzzle box and ended when the cat exited the box. Evaluation of the learning curves (time to escape as a function of trial number) led Thorndike to conclude that the learning was gradual and stochastic. There was no evidence of sudden jumps in performance. Thorndike summarized this observation with the law of effect: Choices that have led to good outcomes in the past are more likely to be repeated in the future. Studies that use the clicking paradigm reveal a similar pattern. Subjects tend to select the alternative that led to good outcome in the past, and the learning curves appear to reflect a gradual and stochastic process. Figure 10.2 demonstrates this pattern. Each curve in this figure summarizes the behavior of 1 participant in the first 25 trials of a simple experiment. The experiment involved a trivial choice task: one option, referred to as H (high payoff) always provided a payoff of 1 shekel, and the second option

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always led to a payoff of 0. The experiment used the basic clicking paradigm. That is, the participants did not receive prior information concerning the payoff rule and could rely on feedback concerning the obtained and forgone payoffs. The results, presented in 5 blocks of 5 trials each, reveal that by the last block, all 3 subjects learned to prefer the better option (H). Yet, the learning process is noisy. For example, the proportion of optimal choices of the “circle” subject go up to 100% by the second block, then go down to 60% in the third block, and then go up to 100% in the fifth block. An ecological justification: Exploration. Recall that the current analysis focuses on conditions that minimize the value of exploration. The agents’ actions did not affect their feedback. However, the subjects could not know with certainty that this is the case. Thus, the observed deviations from “best reply to past experience” can be an indication of exploring the effect of selecting the 0 key. 1.1.2 THE PAYOFF VARIABILITY EFFECT Myers and Sadler (1960) studied decisions from experience using a “card-flipping” paradigm. In each trial of their studies, the participant saw one side of a card and had to decide whether to accept the payoff written on that side (the safe alternative), or the payoff written on the unobserved side of the card (the riskier option). Participants received feedback concerning their payoffs after each choice (the card was flipped only if the participant chose the riskier option). The results revealed that an increase in the payoff variability of the risky option (the variability of the payoff distribution on the unobserved side) reduced the proportion of choices that maximized expected payoff. Busemeyer and Townsend (1993) termed this pattern the “payoff variability effect” and highlighted its robustness. We replicated this pattern in the clicking paradigm with the study of Problems 1, 2, and 3 (the H-rate in the brackets on the right are the proportion of H choices over all trials, and EV is the expected value of the gamble): Problem 1 (r = 200, n = 20, FB = complete, payoff in shekels in a randomly selected trial) H L

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0 with certainty 9 with probability 0.5 −11 otherwise (EV = −1)

[H-rate: 53%]

Problems 1, 2, and 3 were run in the same experiment using a within-participant design. Each of 20 participants (n = 20) faced each problem for 200 rounds (r = 200) under the clicking paradigm with complete feedback (FB = complete). The order of the 3

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10

Blocks of 20 trials Figure 10.3: Proportion of H choices in problems 1–3 in 10 blocks of 20 trials. The results demonstrate the payoff-variability effect.

problems was random. The participants did not receive a description of the problems but were informed that the experiment includes 3 independent parts and when a new part starts. The final payoff for the experiment was the sum of a show-up fee of 30 shekels and the outcome of one randomly selected trial. Notice that problems 1 and 2 involve a choice between alternative H, with an EV of 1 shekel, and alternative L, with an EV of 0. The higher EV maximization rate (H-rate) in problem 1 (96%) compared to problem 2 (58%) is suggestive of risk aversion and/or loss aversion (oversensitivity to losses): H was less attractive (in Problem 2) when it increased the variance and was associated with losses. However, the risk-aversion and the lossaversion explanations are inconsistent with a comparison of problem 2 and problem 3. In problem 3, risk aversion and loss aversion imply maximization (H choices). The results show an H-rate of only 53%. Figure 10.3 presents the observed choice rate of H in blocks of 20 trials. It shows that the differences between the three conditions are relatively robust over time. Additional studies, reviewed in Erev and Barron (2005), demonstrate the robustness of the payoff variability effect. These studies reveal robustness to the payoff sign, to incomplete feedback, and to the number of possible outcomes.5 Chasing, the big eyes effect, and contingent loss aversion. One reasonable explanation of the results in problems 1–3 involves the assertion of large individual differences in risk attitude and/or in the attitude toward losses. For example, the aggregate results are consistent with the hypothesis that about half the participants are risk averse and the other half are risk seekers. However, this explanation has important shortcomings. One clear shortcoming is the fact that the correlation between the R-rate in problems 2 and 3 is not large (see Section 1.1.6). A more interesting shortcoming is suggested by studies

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that examine investment decisions. These studies show that investors tend to “chase” past returns (see Kliger, Levy, and Sonsino 2003; Grinblatt, Titman, and Wermers 1995). That is, they tend to invest in assets that led to high earnings in the past. Grosskopf, Erev, and Yechiam (2006) show that this “big eyes effect” implies that payoff variability can lead most agents to behave as if they are risk seekers. Ben Zion et al. (2010) clarify the robustness of this observation in a study that focuses on the following problem: A simplified investment problem (r = 100, n = 30, FB = complete, 1 point = 0.25¢, pay rule = random trial) R1 R2 S

4x (EV = 0) 2y − 2x (EV = 0) x + y + 5 (the mean of R1 and R2 plus 5, EV = 5)

[S-rate = 25%]

Here, x is a draw from a normal distribution with a mean of 0 and standard deviation of 300 (x ∼ N(0, 300)), and y is a draw from a normal distribution with a mean of 0 and standard deviation of 10 (y ∼ N(0,10)). Ben Zion et al. study can be described as a simulation of a simplified investment task. Options R1 and R2 simulate two risky stocks, and option S simulates an attractive index fund that provides the mean of R1 and R2, plus a small bonus. Thus, option S has the highest mean and lowest variance. The experiment used the clicking paradigm with complete feedback. In addition, the participants received a complete description of the payoff rule. The description emphasized the fact that S provides the mean of R1 and R2 plus 5. The results reveal random choice in the first trial (S-rate of 33%), and a decrease in the tendency to select S with experience. That is, experience with the high payoff variability investment problem impaired maximization. The S-rate in the last block of 20 trials was only 18%. This value is much lower than the 50% rate implied by the assertion that about half of the participants are risk and/or loss averse and lower than the 33% implied under random choice. The correlation effect. Diederich and Busemeyer (1999) highlight an important boundary condition for the payoff variability effect. When the payoffs of the different alternatives are positively correlated, the availability of information concerning foregone payoffs eliminates the payoff variability effect. In the extreme case in which alternative H dominates L in all trials, payoff variability has little effect. Grosskopf, Erev, and Yechiam (2006) demonstrate the robustness of this “correlation effect” in the clicking paradigm. They focused on the following two problems: Problem 4 (r = 200, n = 10, FB = complete, accumulated payoffs 10 units = 0.01 shekel) H L

N(120, 10) + c t (EV = 120) N(100, 10) + dt (EV = 100)

[H-rate: 75%]

Problem 5 (same procedure as in Problem 4) H L

N(120, 10) + c t (EV = 120) N(100, 10) + c t (EV = 100)

[H-rate = 98%]

The exact payoffs were the rounded sum of two terms: A draw from a normal distribution with a mean of 100 or 120 and standard deviation of 10, and (c t or dt ), a

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draw from the distribution (−50 with p = 13 ; 0 with p = 13 ; +50 otherwise). The values of c t and dt were independent. Thus, the payoffs of the two alternatives are positively correlated in problem 5 but are not correlated in problem 4. The feedback after each trial was complete: The participants saw the obtained and the forgone payoffs. The final payoff was the sum of the obtained payoffs, with the conversion rate of 1 shekel per 1,000 points. The results show a clear correlation effect. The correlation increased the maximization rate from 75% (in problem 4) to 98% (in problem 5). Thus, when the correlation is high, subjects can learn to maximize expected return. Probability learning, matching, and overmatching. Many of the early studies of decisions from experience used the probability-learning paradigm. In each trial of a typical study, the participants are asked to guess if a target lightbulb will flash. The probability of a flash is kept constant throughout the experiment. Correct predictions lead to a small gain, and incorrect predictions lead to a lower payoff (0 or a small loss). Grant, Hake, and Hornseth (1951) found an almost perfect match between the true flash probability and the probability of the choice of yes in trials 55 to 60 of their “training phase.” For example, when the probability of a flash was 0.75, the proportion of yes choices in the last block was 75%. Notice that this behavior reflects deviation from maximization: when the probability of flash is 0.75, maximizing reinforcement requires 100% yes choices. This deviation from maximization, known as probability matching, triggered influential studies and lively debates (see Estes 1950, 1964; Bush and Mosteller 1955; Suppes and Atkinson 1960; Edwards 1961; Siegel and Goldstein 1959; Lee 1971; and recent analysis in Bereby-Meyer and Erev 1998; Vulkan 2000; Shanks, Tunney, and McCarthy 2002). The accumulated results demonstrate that probability matching is not a steady state. That is, longer experience slowly moves choice toward maximization. It seems that behavior reflects overmatching: it falls between probability matching and maximization. In animal studies as well (e.g., Sutherland and Mackintosh 1971; Kagel Battalio, and Green 1995), the frequency with which the better alternative is chosen usually exceeds the probability of reinforcement of that alternative. These results imply that behavior in probability learning tasks can be described as an example of the payoff variability effect: when the payoff variability is large, learning is slow and the decision makers do not learn to maximize expected return. A demonstration of the common findings using the basic clicking paradigm is provided with the study (Ert and Bereby-Meyer, forthcoming) of the following problem: Problem 6 (r= 500, n = 20, FB = complete, accumulated payoffs, 1 unit = 0.01 shekel) H L

4 if event E occurs; 0 otherwise (EV = 2.8) 4 if event E does not occur; 0 otherwise (EV = 1.2)

[H-rate: 90%]

Here P (E) = 0.7 The observed H-rate was 70% in the first 50 trials, around 90% between trials 51 and 150, and 93% between trial 401 and trial 500. An ecological justification: Reliance on small samples and similarity based reasoning. The payoff variability and correlation effects can be captured with the assertion that the subjects tend to rely on small samples of past experiences (see Erev and Barron (2005) and related observations in Fiedler (2000); Kareev (2000); Osborne and Rubinstein (1998)). For example, a subject that relies on a sample of 4 observations in trial t,

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recalls 4 past trials and selects the option that led to the best mean payoff in these trials. The expected H-rate (proportion of H choices) of this hypothetical subject is 100% in problem 1, 69% in problems 2 and 3, 74.6% in problem 4, 99.8% in problem 5, and 90% in problem 6. Reliance on small samples is ecologically reasonable under two common conditions. First, in many settings, reliance on small samples saves cognitive efforts (Fiedler 2000; Hertwig and Pleskac 2010; Kareev 2000). It is easier to recall small samples, and it is easier to reach clear conclusions. This cognitive benefit is particularly clear when people rely on the small set of the most recent past experiences. A second set of common conditions in which reliance on small samples is reasonable involves situations in which the payoff rule depends on the state of the word, and the world can be in one of many states. The optimal strategy in this setting requires a focus on past experiences that were obtained under the current state and giving less attention to other past experiences. Whereas this strategy requires a rich memory based on complex computations, people appear to follow it (see Gonzalez, Lerch, and Lebiere 2003; Plonsky, Teodorescu, and Erev 2015). And when the state of the world does not change (the situations just considered) it can lead to deviations from maximization. 1.1.3 UNDERWEIGHTING OF RARE EVENTS AND THE EXPERIENCE-DESCRIPTION GAP Kahneman and Tversky (1979) demonstrate that two of the best-known violations of mainstream economic theory, the tendency to buy both insurance and lotteries (Friedman and Savage 1948) and the Allais paradox (Allais (1953) and the next section), can be explained as indications of overweighting of rare events. Their influential analysis includes two steps: They first replicated the classical violations in a standardized experimental paradigm and then proposed a model (prospect theory) that captures the two phenomena. Prospect theory captures the two phenomena with the assumption of a weighting function that reflects oversensitivity to rare events (events whose probability is below 0.25). The standardized paradigm used by Kahneman and Tversky focuses on “decisions from description”: the subjects were presented with a precise description of two prospects and were asked to select (once, and without any feedback) the prospect they prefer. Barron and Erev (2003) have examined if these phenomena also emerge in the clicking paradigm. Their original hypothesis was that experience will reduce the magnitude of the deviations from maximization. The results surprised them: In several of the problems that they examined, experience did not enhance maximization. In some cases, experience led to a reversal of the deviations captured by prospect theory: It triggered underweighting of rare events. This pattern is known as the experiencedescription gap (see the review in Hertwig and Erev 2009). Problems 7 and 8 demonstrate the evidence for underweighting of rare events in decisions from experience. These problems were studied by Nevo and Erev (2012) using the clicking paradigm with complete feedback. The participants were paid (in shekels) for one randomly selected trial: Problem 7 (r = 100, n = 48, FB = complete, payoff in shekels in a randomly selected trial) S R

0 with certainty +1 with probability 0.9; −10 otherwise (EV = −0.1)

[S-rate = 43%]

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Problem 8 (same procedure as in Problem 7) S R

0 with certainty +10 with probability 0.1; −1 otherwise (EV = +0.1)

[S-rate = 72%]

Notice that in problem 7, the safer option has higher expected value, but the participants tend to select the gamble. Problem 8 reflects the opposite risk preference: The gamble has higher expected value, but the participants tend to select the safer option. As noted by Barron and Erev, this pattern can be a reflection of insufficient sensitivity to the rare and extreme outcomes that occur in 10% of the trials. Thus, the participants behave as if they believe that “it won’t happen to me.” The reversed certainty effect (reversed Allais paradox). A clear demonstration of the significance of the difference between decisions from experience and decisions from description is provided by the study of variants of Allais’ (1953) common ratio problems. Expected utility theory (von Neumann and Morgenstern 1947) implies that if prospect B is preferred to A, then any probability mixture (B, p) must be preferred to the mixture (A, p).6 In his classic experiment, Allais (1953) found a clear violation of this prediction. He constructed an example in which the more risky of two prospects becomes relatively more attractive when the probability of winning in both prospects is transformed by a common ratio. Kahneman and Tversky (1979) refer to this pattern as the “certainty effect.” Barron and Erev (2003) demonstrate that decisions from experience (in the clicking paradigm with incomplete feedback) reflect the opposite pattern. The study of problems 9 and 10 replicates these results using the clicking paradigm with complete feedback: Problem 9 (r = 400, n = 24, FB = complete, accumulated payoff 1 point = 0.01 shekel) S R

3 with certainty 4 with probability 0.8; 0 otherwise (EV = 3.2)

[S-rate = 36%]

Problem 10 (same procedure as in Problem 9) S R R

3 with probability 0.25; 0 otherwise (EV = 0.75) 4 with probability 0.2; 0 otherwise (EV = 0.80)

[S-rate = 51%]

The results reveal a reversed certainty effect. The safe option (S) was less attractive in problem 9—when it was associated with certainty—than in problem 10—when it was not. This pattern is consistent with the assertion that in decisions from experience, the least likely events (probability of 0.2) are underweighted. Additional studies of the certainty effect reveal differences between rats, bees, and human subjects. MacDonald et al. (1991) show that rats exhibit the original certainty effect: They studied variants of problems 9 and 10 with payoffs in cups of water and found more S choices when S provides medium pay with certainty. In contrast, Shafir et al. (2008) show that honeybees exhibit the reversed certainty effect. Their study examined variants of problems 9 and 10 with payoffs in terms of the percentage of sugar

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water and found fewer S choices when S provides medium pay with certainty. Shafir et al. suggested that perceptual noise might be responsible. According to this explanation, the rats (but not the bees) had difficulty in discriminating the medium and high payoffs and for that reason preferred S in the variant of problem 9. The value of this explanation was demonstrated in a study with human subjects, which revealed that a reduction in the clarity of the feedback (in a study of problems 9 and 10) leads to the emergence of the original certainty effect. Underweighting and overestimation. The suggestion that people underweight rare events appears to be inconsistent with previous research that demonstrates overestimation of rare events (e.g., Viscusi 2002; Erev, Wellsten, and Budescu 1994). For example Viscusi (2002) found that both smokers and nonsmokers tend to overestimate the probability that smokers will develop lung cancer. Barron and Yechiam (2009) examined whether this difference between smokers and nonsmokers is mediated by different settings (e.g., clicking vs. smoking) or different tasks (deciding or estimating). They studied problem 11 using the clicking paradigm with complete feedback and one addition: starting at trial 201, the participants were asked to estimate the probability of the rare outcome (1 point with probability 0.15) before each choice. The results reveal a strong tendency to prefer the risky prospect (R) in all 400 trials (mean R-rate of 79%). This result is consistent with underweighting of rare events. The estimations, on the other hand, reflected oversensitivity to rare events. The average estimate (of the 15% event) was 21%. Thus, participants appear to exhibit oversensitivity to rare events in estimation, and undersensitivity to rare events in choice (similar results are reported by Friedman and Massaro, 1998). Problem 11 (r = 400, n = 24, FB = complete, accumulated payoffs, 1 unit = 0.01 shekel) R S

3 with probability 0.85; 1 otherwise (EV = 2.7) 2.7 with certainty

[R-rate = 79%]

The sampling paradigm and robustness to the number of repeated gamble realizations. Hertwig et al. (2004) note that the “experience-description gap” just summarized can be attributed to two differences between the experimental paradigms: the source of the information (experience or description), and the number of repeated realizations of the gambles (one or many). To evaluate the role of these factors, they examined some of the problems considered by Barron and Erev (2003) under two conditions: one-shot decisions from description and one-shot decisions from experience. The two conditions differed only with respect to how the decision makers learned about the options’ outcomes and likelihoods. In the description group, options were described as in Kahneman and Tversky’s studies. In the sampling group, the information describing the options was not displayed. Instead, participants were shown two buttons on the computer screen and were told that each button was associated with a payoff distribution. Pressing on a given button elicited the sampling of an outcome (with replacement) from its distribution. In problem 9, for example, drawing from one distribution led to the outcome 4 in 80% of all draws and to the outcome 0 in 20% of all draws. Sampling from the other distribution always resulted in the outcome 3. Participants could sample however often they wished. By repeatedly experiencing the contingency between choices and outcomes, participants

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could gradually acquire knowledge about the options’ payoff structure. Once they stopped sampling, they indicated their preferred option, and, after completing all problems, participants received monetary payoffs according to their choices and the outcomes of the draws. The observed choice proportions in the sampling group exhibit the pattern observed under the study of the same problems by Barron and Erev (2003) using the clicking paradigm. That is, the participants behave as if they underweight rare events. The correlation between the sampling and the clicking results was 0.92. The observed choice proportion in the description group exhibits the pattern predicted by prospect theory— the participants behave as if they overweight rare events. The correlation between the sampling and the description group was −0.67. These results (and similar findings reported in Weber, Shafir, and Blais (2004), Ungemach , Chater, and Stewart (2008). Erev, Ert, et al. (2010a), Hau, Pleskac, and Hertwig (2008) and in reviews by Hertwig and Erev (2009) and Rakow and Newell (2010)) suggest that the tendency to underweight rare events can be observed in one-shot decisions from experience. Thus, the distinct information source is a sufficient condition for the experience-description gap. Robustness to prior information. Lejarraga and Gonzalez (2011) have examined the effect of prior information concerning payoff distributions on the tendency to underweight rare events in the clicking paradigm, examining the joint effect of description and experience. In one of their studies, the participants were asked to select between a safe prospect that provides 3 with certainty and a gamble that provides 64 with probability 0.05 and 0 otherwise. Their results reveal that the initial behavior reflects high sensitivity to the rare events, with the emergence of underweighting of rare events with experience. The proportion of gambles chosen between trial 10 and 100 was below 30%. Jessup, Bishara, and Busemeyer (2008) document a similar pattern in a study in which the exact value of the gamble varied from trial to trial. Alternative explanations of the weak effect of description of the incentive structure, in the current setting are discussed in Section 1.1.9. Sensitivity to expected values. An extreme interpretation of the results just summarized would be that decision makers tend to neglect rare events; that is, in most cases they fail to consider these events. Ert and Erev (2016) show a shortcoming of this extreme explanation by examining the following problems: Problem 12 (r = 400, n = 24, FB = complete, accumulated payoffs, 1 unit = 0.01 shekel) H L

2.52 with certainty 2.53 with probability 0.89; 2.43 otherwise (EV = 2.519)

[H-rate = 40%]

Problem 13 (same procedure as in Problem 12) H L

2.52 with certainty 2.53 with probability 0.89; 2.03 otherwise (EV = 2.48)

[H-rate = 72%]

The results show a deviation from maximization consistent with underweighting of rare events in problem 12 but not in problem 13. This pattern suggests that the rare events are not neglected. When they are sufficiently important they are taken into account.7

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Sensitivity to the coefficient of variance. Shafir (2000) reviews experimental studies of animal risk attitude in a binary choice task. The results suggest that under normal conditions the tendency to select the safer alternative is better predicted by the coefficient of variance (CV) than by the variance of the risky alternative. CV is defined as the payoff standard deviation divided by the payoff mean. Weber, Shafir, and Blais (2004) show that this pattern is consistent with underweighting of rare events. Underweighting of rare events implies risky choices when the CV is low (relatively high mean) and risk aversion when the CV is high (relatively low mean). Signal-detection tasks. In binary signal–detection tasks, an observer is asked to classify stimuli that belong to one of two distributions. In a typical experiment (see the review in Erev 1998), the two distributions are normal with equal variance, and they represent the state of the world. For example, the state may be the gender of a candidate (male or female), and the signal may be the candidate’s height. After each response (guessing male or female) the observer receives immediate payoff determined by a fixed 2 × 2 payoff matrix that gives the payoff for each of the four possible outcomes (correct detection of a male, correct detection of a female, incorrect male response, and incorrect female response). Assuming that the male’s mean is higher, the optimal choice rule is a cutoff strategy of the type respond male if the signal exceeds a certain height. The location of the cutoff depends on the payoff of the 4 outcomes and on the prior probability of the two distributions. Experimental studies of this task reveal higher sensitivity to the prior probabilities than to the payoffs (see Healy and Kubovy 1981). Barkan, Zohar, and Erev (1998) show that this pattern implies deviation from maximization in the direction of underweighting rare events. An ecological justification: Sampling and weighting. The tendency to underweight rare events can be explained with the assertion, just presented, that people rely on small samples of past experiences. For example, a subject that relies on a sample of 4 past experiences will prefer the negative EV gamble −10 with probability 0.1, +1 otherwise over 0 with certainty in 56% of the trials (because 65% of the samples of size 4 do not include the 10% event). However, this assumption of strong reliance on small samples cannot explain the observed sensitivity to the expected value in problem 13 (i.e., reliance on a sample of 4 implies the same behavior in problems 12 and 13). The coexistence of underweighting of rare events and some sensitivity to expected values can be captured by a weak variant of the reliance on the small-samples hypothesis: the assumption that a small sample of experiences receives more attention than the other experiences, but all experiences receive some attention. Thus, when the difference in the expected values is large enough, it affects behavior. 1.1.4 THE VERY RECENT AND THE WAVY RECENCY EFFECTS Analysis of the effect of recent outcomes on choice behavior in probability learning tasks led Estes (1964; also see the review in Lee (1971)) to conclude that the most common pattern is positive recency: decision makers are more likely to select the alternative that led to the best outcome in recent trials. A clear example of positive recency in the clicking paradigm is provided in the analysis of the contingent choice rate in problems 2 and 3 in the top panel of Table 10.1. The probability of risky (R) choices is larger, in these problems, after high payoff from R than after low payoff from R. The overall R-rates are 64% after high payoff and 40% after low payoff. Aggregation over the two payoffs (high and low) suggests that that the proportion of choices that are the best reply to the most recent payoff, referred to as Best-Reply-1, is 62%.

S 0 with certainty R 1 with certainty

S 0 with certainty R 1 (11, 0.5; −0.9)

S 0 with certainty R (9, 0.5; −11)

S 0 with certainty R (10, 0.1; −1)

S 0 with certainty R (1, 0.9; −10)

S 3 with certainty R (4, 0.8; 0)

1 [200]

2 [200]

3 [200]

4 [100]

8 [100]

9 [400]

Problem [Number of trials]

R-rate Recency

R-rate Recency

R-rate Recency

R-rate Recency

R-rate Recency

R-rate

Most recent payoff from R

Last choice

0.2

0.21

0.23

0.40

0.56

0.43

High —

0.20 +0.06

0.31 −0.10

0.06 +0.17

0.16 +0.24

0.21 +0.35

—

Low

S (R-rate is switch rate, recent payoff from R is forgone)

0.91

0.84

0.60

0.77

0.81

0.99

High —

0.67 +0.24

0.69 +0.15

0.79 −0.19

0.60 +0.17

0.59 +0.22

—

Low

R (R-rate is repetition rate, recent payoff from R is obtained)

Experimental Results R-Rates and Implied Recency Effect as a Function of Last Choice and Recent Payoff from R

0.64

0.56

0.29

0.47

0.58

0.96

R-Rate over All Trials

0.36

0.24

0.32

0.24

0.37

0.48

High

—

0.38 −0.02

0.26 −0.02

0.13 +0.19

0.18 +0.06

0.30 +0.07

—

Low

0.85

0.87

0.74

0.72

0.81

0.94

High

—

0.76 +0.09

0.68 +0.19

0.76 −0.02

0.64 +0.08

0.76 +0.05

—

Low

The Predictions of I-SAW R-Rates and Implied Recency Effect as a Function of Last Choice and Recent Payoff from R Last Choice S R (R-rate is switch (R-rate is repetition rate, recent payoff rate, recent payoff from R is forgone) from R is obtained)

0.68

0.62

0.38

0.40

0.61

0.89

R-Rate over All Trials

TABLE 10.1: Summary of experiments that examine a choice between a safe prospect and a prospect with no more than two outcomes using the basic clicking paradigm. The recency effects (in bold) are estimated as the difference between the R-rates after high and low payoffs from R given the same recent choice.

R-rate Recency R-rate Recency R-rate Recency R-rate Recency R-rate Recency

S 7 with certainty R (16.5, 0.01; 6.9)

S −9.4 with certainty R (−2, 0.05; −10.4)

S −4.1 with certainty R (1.3, 0.05; −4.3)

S −18.7 with certainty R (−7.1, 0.07; −19.6)

S −7.9 with certainty R (5, 0.08; −9.1)

14 [100]

15 [100]

16 [100]

17 [100]

18 [100]

R-rate Recency

S 2.52 with certainty R (2.53, 0.89; 2.03)

13 [400]

R-rate Recency

S 2.52 with certainty R (2.53, 0.89; 2.43)

Most recent payoff from R

Last choice

12 [400]

Problem [Number of trials]

TABLE 10.1: Continued.

0.20

0.29

0.27

0.15

0.40

0.06

0.15

High

0.06 +0.14

0.06 +0.23

0.06 +0.21

0.06 +0.09

0.04 +0.36

0.08 −0.02

0.09 +0.06

Low

S (R-rate is switch rate, recent payoff from R is forgone)

0.86

0.85

0.86

0.70

0.94

0.92

0.94

High

0.84 +0.02

0.87 −0.02

0.94 −0.08

0.80 −0.10

0.95 −0.01

0.63 +0.29

0.78 +0.16

Low

R (R-rate is repetition rate, recent payoff from R is obtained)

Experimental Results R-Rates and Implied Recency Effect as a Function of Last Choice and Recent Payoff from R

0.31

0.38

0.54

0.26

0.45

0.28

0.60

R-Rate over All Trials

0.30

0.31

0.36

0.23

0.46

0.08

0.28

High

0.08

0.12 +0.18

0.11 +0.20

0.11 +0.25

0.09 +0.14

0.07 +0.39

0

0.30 −0.02

Low

0.71

0.72

0.81

0.56

0.77

0.76

0.85

High

0.75 −0.04

0.76 −0.04

0.84 −0.03

0.71 −0.15

0.91 −0.14

0.57 +0.19

0.72 +0.13

Low

The Predictions of I-SAW R-Rates and Implied Recency Effect as a Function of Last Choice and Recent Payoff from R Last Choice S R (R-rate is switch (R-rate is repetition rate, recent payoff rate, recent payoff from R is forgone) from R is obtained)

0.34

0.35

0.42

0.26

0.46

0.24

0.63

R-Rate over All Trials

R-rate Recency

S −15.5 with certainty R (−8.8, 0.6; −19.5)

S 2.2 with certainty R (3, 0.93; −7.2)

S 25.2 with certainty R (26.5, 0.94; 8.3)

S 6.8 with certainty R (7.3, 0.96; −8.5)

S 11 with certainty R (11.4, 0.97; 1.9)

21 [100]

22 [100]

23 [100]

24 [100]

25 [100]

R-rate Recency

R-rate Recency

R-rate Recency

R-rate Recency

R-rate Recency

S 11.5 with certainty R (25.7, 0.1; 8.1)

20 [100]

R-rate Recency

S −25.4 with certainty R (−8.9, 0.08; −26.3)

Most recent payoff from R

Last choice

19 [100]

Problem [Number of trials]

TABLE 10.1: Continued.

0.09

0.08

0.14

0.13

0.42

0.29

0.22

High

0.19 −0.10

0.23 −0.15

0.32 −0.18

0.15 −0.02

0.19 +0.23

0.07 +0.22

0.07 +0.15

Low

S (R-rate is switch rate, recent payoff from R is forgone)

0.94

0.92

0.86

0.85

0.91

0.81

0.89

High

0.71 +0.23

0.77 +0.15

0.82 +0.04

0.68 +0.17

0.75 +0.16

0.78 +0.03

0.90 −0.01

Low

R (R-rate is repetition rate, recent payoff from R is obtained)

Experimental Results R-Rates and Implied Recency Effect as a Function of Last Choice and Recent Payoff from R

0.57

0.50

0.52

0.47

0.68

0.30

0.45

R-Rate over All Trials

0.19

0.16

0.25

0.25

0.44

0.23

0.35

High

0.33 −0.14

0.21 −0.05

0.31 −0.06

0.30 −0.05

0.39 +0.05

0.11 +0.12

0.13 +0.22

Low

0.92

0.90

0.90

0.89

0.90

0.60

0.82

High

0.70 +0.22

0.65 +0.25

0.71 +0.19

0.71 +0.18

0.86 +0.04

0.67 −0.07

0.83 −0.01

Low

The Predictions of I-SAW R-Rates and Implied Recency Effect as a Function of Last Choice and Recent Payoff from R Last Choice S R (R-rate is switch (R-rate is repetition rate, recent payoff rate, recent payoff from R is forgone) from R is obtained)

0.68

0.60

0.68

0.67

0.77

0.26

0.46

R-Rate over All Trials

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0.7 0.6 0.5

0.3

BR rate

0.4

0.2 0.1 20 19 18 17 16 15 14 13 12 11 10 9

8

7

6

5

4

3

2

1

0

0

Lag Figure 10.4: The very recent effect in problems 2 and 3: the proportion of choices (at trial t) of the alternative that led to the best outcome in trial t-Lag. Thus, Lag = 1 (on the right) presents the best reply rate to the most recent trial.

An extension of this analysis to other recent outcomes reveals an interesting pattern. To describe this pattern, let Best-Reply-L be the choice rate of the alternative that led to the best outcomes exactly L trials before the current trial. Figure 10.4 presents the values of Best-Reply-1 to Best-Reply-20 (based on data from trials 21 up to 200 in problems 2 and 3). The results reveal a large qualitative difference between BestReply-1 and the other values. The decrease in the effect of recent outcomes appears to be sharp. Best-Reply-1 reflects a strong recency effect, but Best-Reply-2 and -3 are not larger than the mean value. Indeed, Best-Reply-3 is the lowest point in the curve in Figure 10.4. Nevo and Erev (2012) refer to this pattern as the very recent effect. Plonsky, Teodorescu, and Erev (2015) show that deviation from positive recency is even larger in problems with rare events: the recency curve is problems of this type tend to be wavy. An ecological justification: State inertia. The unique effect of the most recent outcome can be captured with the assertion that in some trials the decision makers behave as if they assume that the payoff rule is determined by the state of nature, and the current state is not likely to change (the state in the next trial is likely to be identical to the state in the last trial). 1.1.5 INERTIA AND SURPRISE-TRIGGERS-CHANGE Analysis of the relationship between recent and current choice reveals strong positive correlation that implies inertia (Nevin 1988; Cooper and Kagel 2008; Suppes and Atkinson 1960, Erev and Haruvy 2005). Decision makers tend to repeat their last choice. For example, over problems 2 and 3, the participants repeated their last choice in 68% of the trials. Moreover, inertia is a better predictor of behavior than positive recency. When inertia and positive recency lead to contradicting predictions, the decision makers are more likely to exhibit inertia (as noted in Section 1.1.4, the positive recency rate is only 62%). Overalternation. Previous research highlights two boundary conditions for inertia. First, in some cases human decision makers exhibit overalternation when they are asked to select between alternatives that are known to be identical (see Rapoport and Budescu (1997) and Section 4.2.2). Second, animal studies (see review in Dember and Fowler

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1958) highlight spontaneous alternation by certain species in certain settings that can be described as a response to an environment in which inertia is counterproductive. Negative recency. The first row in Table 10.1 presents the choice rates in problems 7 and 8 by the last choice and the recent payoffs. The results reveal two deviations from positive recency. The first deviation emerges in problem 8 after choice R. The rate of repeated R choice was 79% after a loss (the payoff −1), and only 61% after a gain (payoff of +10). The second indication of negative recency is observed in problem 7 after choice S. The rate of a switch to R was 31% after a forgone loss (the payoff −10), and only 21% after a forgone gain (payoff of +1). The lower rows in Table 10.1 demonstrate that this pattern is not unique to problems 7 and 8. It presents the results obtained in the study of 12 additional problems by Nevo and Erev (using the basic clicking paradigm). Most problems reveal higher change rates after surprising outcomes, even when the surprising outcomes reinforce the last choice. The relative effect of obtained and foregone outcomes. Under an extreme interpretation of Thorndike’s (1898) law of effect, behavior is driven by obtained outcomes. Thus, information concerning foregone payoffs is not likely to have a significant effect. However, experimental evaluations of this hypothesis show that it can be rejected (e.g., Mookherjee and Sopher 1994, 1997; Camerer and Ho 1999; Nyarko and Schotter 2002; Marchiori and Warglien 2008). In fact, in certain settings people are more sensitive to foregone than to obtained outcomes (e.g., Grosskopf, Erev, and Yechiam 2006). The results, presented in Table 10.1, reveal a similar pattern: the best reply rate to the forgone payoff is larger than the best reply rate to the obtained payoff. One boundary condition to the current observation involves the number of alternatives. When the number of alternatives is very large, people are more likely to pay attention to the payoff of the alternative they chose than to the forgone payoff from each of the other multiple alternatives (see Ert and Erev 2007). An ecological justification: Action inertia and surprise-trigger-change. The observed inertia and the complex recency pattern documented in Table 10.1 can be captured with the hypothesis that in certain trials people choose an inertia mode and simply repeat their last choice. This tendency is ecologically reasonable when the cost of deciding is larger than the expected benefit. Specifically, if the agent carefully reached a decision before trial t, making another costly decision at trial t is likely to be cost effective only if the recent feedback is surprising. 1.1.6 INDIVIDUAL DIFFERENCES AND THE IOWA GAMBLING TASK While studying patients with neuropsychological disorders, Bechara et al. (1994) have found that a specific neurological syndrome is associated with poor performance in a simple decision-from-experience task. The population they studied involved patients with lesions in the orbitofrontal cortex. This syndrome involves intact IQ and reasoning skills but poor decision-making capacities. The task they proposed for assessing decision capacities is now known as the Iowa gambling task. It is presented as a choice between four decks of cards. Each alternative results in one of two outcomes: a sure gain and some probability of a loss. The implied payoff distributions (the sum of the two outcomes) are as follows. The Iowa gambling task: Dis. R: Win $100 with probability 0.9; lose $1150 otherwise (EV = −25) Dis. S: Win $100 with probability 0.5; lose $150 otherwise (EV = −25)

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Adv. R: Win $50 with probability 0.9; lose $200 otherwise (EV = +25) Adv. S: Win $50 with probability 0.5; 0 otherwise (EV = +25) As in the clicking paradigm, the decision makers do not receive a description of the different distributions. Their information is limited to the obtained payoff after each trial. The experiment included 100 trials. Notice that two of the alternatives are advantageous (Adv. R and Adv. S have expected payoff of 25), and two are disadvantageous (Dis. R and Dis. S have expected value of −25). Bechara et al. found that the patients with lesions in the orbitofrontal cortex did not learn to avoid the disadvantageous alternatives, while the participants in the control groups (patients with other neurological problems) did. Following up on these findings, Busemeyer and Stout (2002) presented a simple reinforcement learning model that implies that the failure to learn in the Iowa gambling task can be a product of three different behavioral tendencies: overexploration, a recency effect, and insufficient sensitivity to losses. Under Busemeyer and Stout’s model, these three tendencies are abstracted as parameters that can be estimated from the data. Yechiam et al. (2005; 2008) showed the value of this approach. For example, they showed that the estimation of the learning parameters can be used to distinguish between criminals. In their study of first-time offenders at the reception and classification facility for the State of Iowa Department of Corrections, diverse criminal subgroups all performed poorly in the Iowa gambling task. However, it was found that criminals incarcerated for drug addiction or repeat sex offenders showed insufficient sensitivity to losses. In contrast, more-violent criminals, including those convicted of assault and/or murder—and to some extent those convicted of robbery as well— exhibited high recency. An additional indication of the significance of individual differences is provided by the analysis of the correlation between behavior in problems 2 and 3 in the clicking experiment described earlier. Recall that the experiment used the basic clicking paradigm, and 20 participants faced both problems. Following Yechiam et al. (2005), we focused on three variables: the proportion of risky choices (a measure of attitude toward losses), the proportion of Best-Reply-1 (a measure of a recency effect), and the distance between the mean choice rate and 0.5 (a measure of decisiveness). The observed correlations are 0.18, 0.75, and 0.69 for loss attitude, recency, and decisiveness (with the last two values highly significant). An ecological justification: Variability facilitates evolution and learning. The existence of variability is a necessary condition for survival in a number of instances, so it would be selected in the evolutionary process. Another attractive feature of variability in learning is the fact that it can facilitate coordination. Specifically, variability enhances efficiency in coordination games in which the payoff decreases with the number of people that make the same choice. One example is the market-entry game described later. 1.1.7 QUANTITATIVE SUMMARY: INERTIA, SAMPLING, AND WEIGHTING (I-SAW) Nevo and Erev (2012) propose a descriptive model that can reproduce the six behavioral regularities just presented. The model, referred to as I-SAW, can be described by the following assumptions. I-SAW1: Three response modes. The model distinguishes between three response modes: exploration, exploitation, and inertia. Exploration is assumed to imply random

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choice. The probability of exploration by individual i is set to 1 in the first trial and εi (a trait of i ) in all other trials. During exploitation trials, individual i selects the alternative with the highest estimated subjective value (ESV). The ESV of alternative j in trial t > 1 is ESV( j, t) = (1 − wi )(S_Mean) + wi (G_Mean)

(1)

where S_Mean (sample mean) is the average payoff from alternative j in a small sample of μi previous trials in similar settings, G_Mean (grand mean) is the average payoff from j over all (t − 1) previous trials, and μi and wi are traits. The assumed reliance on a small sample from experience is introduced to capture underweighting of rare events and the payoff variability effect (see similar abstractions in and related ideas in Osborne and Rubinstein 1998; Fiedler 2000; Kareev 2000; Rapoport and Budescu 1997; Hertwig et al. 2004; Lebiere, Gonzalez, and Martin 2007). The assumed sensitivity to the grand mean was introduced (following a similar assumption in Gonzalez et al. 2003) to capture the observed sensitivity to expected values. I-SAW2: Similarity and recency. The μi draws are assumed to be independent (sampling with replacement) and biased toward the most recent experience (trial t − 1). A bias with respect to trial t − 1 occurs with probability ρi (a trait). The remainder of the time (probability 1 − ρi ), the agent relies on experience from the trials that appear to be most similar to the current trial. When all the previous trials are objectively equally similar (the current case), the apparent similarity criterion implies random choice. The motivation behind the recency bias is the “very recent effect.” I-SAW3: Surprise-triggers-change. Inertia is added with the assumption that the individuals tend to repeat their last choice. The exact probability of inertia at trial t + 1 is assumed to decrease when the recent outcomes are surprising. Specifically, if the exploration mode was not selected, the probability of inertia is surprise(t)

P (inertia at t + 1) = πi

(2)

where 0 ≤ πi < 1 is a trait that captures the tendency for inertia. The value of the surprise term is assumed to equal the average of four gaps between certain expectations and the obtained payoffs. In the first two (one for each alternative), the assumed expectation is that the last payoff will be obtained again; thus the gap is between the payoff at t− 1 and the payoff at t. In the last two, the assumed expectation is the mean payoff; thus, the gap is between the grand mean and the payoff at t. Specifically, ⎡ 2  1   obtained j (t − 1) − obtained j (t) gap(t) = ⎣ 4 j =1 ⎤ 2    G _mean j (t) − obtained j (t)⎦ +

(3)

j =1

where obtained j (t) is the payoff obtained from j at trial t, and G _mean j (t) is the average payoff obtained from j in the first t − 1 trials (the grand mean). The surprise

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at t is normalized by the mean gap (in the first t − 1 trials): surprise(t) =

gap(t) [mean_gap(t) + gap(t)]

(4)

The mean gap at t is a running average of the gap in the previous trials (with mean_gap(1) = 0.00001). Specifically, mean_gap(t + 1) = mean_gap(t)(1 − 1/r ) + gap(t)(1/r )

(5)

where r is the expected number of trials in the experiment (100 in the current study). Notice that the normalization (equation 4) implies that the value of surprise(t) is between 0 and 1, and the probability of inertia is between πi (when surprise(t) = 1) and 1 (when surprise (t) = 0). An interesting justification for this gap-based abstraction comes from the observation that the activity of certain dopamine-related neurons is correlated with the difference between expected and obtained outcomes (see Schultz (1998) and related analysis in Caplin and Dean (2007)). I-SAW4: Individual differences, traits, and parameters. The traits are assumed to be independently drawn from a uniform distribution between the minimal possible value (allowed by the model) and a higher point. Thus, the model has 5 free parameters: the highest point of the 5 distributions. Estimation and results. We used a grid-search procedure to estimate the parameters of the model. The criterion was the mean-squared deviation (MSD) between the model’s predictions and the experimental results (including the results summarized in Table 10.1). That is, we ran computer simulations to derive the predictions of the model under different parameters and selected the parameters that minimize the MSD score. The estimated parameters imply the following trait distribution: εi ∼ U [0, 0.24], wi ∼ U [0, 1], ρi ∼ U [0, 0.12], πi ∼ U [0, 0.6], and μi = 1, 2, 3, or 4. The right-hand columns in Table 10.1 present the predictions of I-SAW with these parameters. The results reveal that I-SAW reproduces all the behavioral tendencies documented in Table 10.1. In addition, the model provides good quantitative fit. For example, the correlation between the predicted and the observed aggregate choice rates is 0.9, and the MSD score is 0.007. Additional evaluations of this model are discussed in Sections 1.3 and 4.2. 1.1.8 IMPLICATIONS OF I-SAW RELATIVE TO TRADITIONAL REINFORCEMENT LEARNING AND F ICTITIOUS P LAY M ODELS I-SAW can be described as an example of a reinforcement-learning model (see Satton and Barto 1998; Roth and Erev 1995) and as a generalization of the fictitious play rule (Brown 1951; Robinson 1951; Fudenberg and Levine 1998) and of the naïve sampler model (Erev and Roth 2014). The following section clarifies these connections. Fictitious play (FP). The FP rule assumes that the decision maker tries to maximize expected return under the assumption that the payoff distributions are static. This assumption is fictitious in many settings, but it is correct in the basic clicking paradigm. At trial t>1, this rule implies a selection of the alternative that led to the highest average payoff in the first t − 1 trials (and random choice is assumed at t = 1). I-SAW implies FP with the traits: εi = 0, wi = 1, ρi = 0, and πi = 0. That is, under the FP rule, the estimated subjective value is the grand mean (G_mean), and the alternative with the highest G_mean is selected. The correlation between the aggregate choice rate and

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the model with these parameters is 0.76, and the MSD score is 0.039. These results suggest that the FP rule (and the implied maximization assumption) provides a useful approximation of the results, but the I-SAW generalization of this rule provides a much better approximation. Additional analysis reveals that the advantage of the generalized model over the FP rule decreases when the difference between the average payoffs from the different alternative is large (relatively to the payoff variability); when this relative difference is large enough the predictions of I-SAW are identical to the predictions of the FP rule. Stochastic fictitious play (SFP). The SFP model (Cheung and Friedman 1997, 1998) is a generalization of the FP rule that allows for the possibility that the estimated subjective value of option j at trial t includes error. That is, ESV( j, t) = G_mean( j, t) + ε j t

(6)

The traditional implementation adds the assumption that the error terms are randomly, identically, and independently distributed. It is convenient to assume that this distribution follows a type I extreme value distribution, which approximates the normal distribution. As demonstrated by McFadden (1974), this assumption implies that the probability of preferring j over k at trial t is P ( j, t) =

1 1 + e σ [G_mean(k,t)−G_mean( j,t)]

(7)

SFP can be described as a variant of I-SAW with the parameters εi = 0, wi = 0.5, ρi = 0, and πi = 0 and with a modified error term. The error term under I-SAW is determined by a draw of μi past experiences. The I-SAW error term is less convenient to model (as it does not allow the derivation of the elegant choice probability term implied under a normal error), but it appears to fit the data better. The advantage of the I-SAW error term is clarified by a comparison of problems 1 and 2. I-SAW implies no error in problem 1 (the trivial no variability problem), and high error rate in problem 2. The SFP allows for the possibility of different error terms by assuming situation specific σ values but cannot predict a long-term difference between the two problems without problem specific parameters. Reinforcement learning. Simple reinforcement learning models were found to provide good ex ante predictions of behavior in certain games (Erev and Roth 1998), to imply maximization in certain settings (Sutton and Barto 1998), and to be consistent with known activities of the brain (Schultz 1998). In order to clarify the relationship of these models to the current results, it is important to recall that the term reinforcement learning is used to describe a very large set of models (Dayan and Niv 2008). I-SAW is a member of this class of models. We believe that the most important difference between I-SAW and the popular reinforcement-learning model involves the error term discussed earlier. Like the SFP model, the popular reinforcement-learning models assume a normal error term. Other differences between I-SAW and the popular reinforcementlearning model involve the surprise trigger change assumption, and the abstraction of the recency effect. These new factors were introduced to capture the 6 phenomena summarized in Section 1.1 and are evaluated in the two choice-prediction competitions described in Section 1.3. The naïve sampler model and probability matching. The naïve sampler model assumes random choice at the first trial and then reliance on a sample of size μi (property the

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agent) with replacement from all past experiences. It is an example of I-SAW with the constraints εi = 0, wi = 0, ρi = 0, πi = 0. The naïve sampler model captures the payoff variability effect, and underweighting of rare events, but cannot capture the other phenomena listed above. Best fit with these constraints is obtained with μi = 1, 2, 3, . . . , 14. The correlation between the aggregate choice rate and the model with these parameters is 0.83, and the MSD score is 0.019. With the additional constraint μi = 1, I-SAW implies the “probability matching” rule (matching the choice rate to the probability of success (see Estes 1950; Blavatskyy 2006). The correlation between the aggregate choice rate and the model with these parameters is 0.56, and the MSD score is 0.093. 1.1.9 ALTERNATIVE EXPLANATIONS OF THE EXPERIENCE-DESCRIPTION GAP Prospect theory (Kahneman and Tversky 1979; Wakker 2010), the leading model of decisions from description, captures three main behavioral regularities: overweighting of rare events, loss aversion, and the reflection effect (risk aversion in the gain domain and risk seeking in the loss domain). The results reviewed earlier show that different regularities emerge in the study of decisions from experience. The results reflect underweighting of rare events (Section 1.1.3), with no consistent indication for loss aversion (Section 1.1.2). In addition, under certain settings decisions from experience reveal a reverse reflection effect (Ludvig and Spetch 2011). Recent research suggests several explanations for these differences. Our favorite explanation involves the assertion that decisions from description are a subclass of the larger class of decisions from experience. As in other subclasses, the decision makers tend to select strategies that have led to good outcomes in similar situations in the past. The experience-description gap emerges, under this explanation, as a result of two main effects of the available description. First, in certain cases, the description affects the set of strategies that can be used (see related ideas in Busemeyer and Myung 1992; Erev 1998; Rieskamp and Otto 2006; Erev and Roth 2001; Stahl 1996, 1999, 2000; Erev and Barron 2005). Second, the description affects the set of past experiences perceived to be similar. In order to clarify the assertion that the description can affect the set of strategies, consider the following hypothetical choice problem: Thought Experiment 1. Choose between H L

0 with certainty $1 with probability 0.99, −$1,000,000 otherwise

It is easy to see that the availability of a description of the incentive structure will have a large effect here. Without a description (if this problem would be studied using the basic clicking paradigm), people are likely to select L at least until the first loss. With a description, reasonable individuals are expected to prefer H. This pattern can be captured with the hypothesis that the current description leads people to follow this rule: compute the expected values implied by the description, and select the best alternative based on this dimension. The apparent inconsistency between this hypothesis and the weak effect of description discussed in Sections 1.1.2 and 1.1.3 can be explained with the assertion that the tendency to use the EV rule decreases when the difference between the expected values, implied by the description, appear to be small and/or when the computation is too difficult (see Payne, Battman, and Johnson 1993). That is, the EV

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strategy is less likely to be used when the problem is similar to problems in which the EV rule was not found to be effective. Marchiori, DiGuida, and Erev (2014) show that the current assertion can be used to explain “overweighting of rare events” in “one-shot decisions from description.” Their explanation adds the assumption of overgeneralization from situations in which people decide based on subjective probability estimates. Subjective probability estimates tend to reflect overconfidence; for example, studies of probability estimates reveal that events estimated to occur 5% of the time actually occur about 20% of the time (Erev, Wallsten, and Budescu 1994). This overconfidence can be the product of random error: some of the events, estimated by probability 5%, occur with different probabilities, and this biases the occurrence rate toward 50%. Thus, the best reply to the belief that events that were estimated to occur with probability 5% will occur with higher probability tends to be reinforcing. Overgeneralization—from decisions with overconfident estimates to decisions under risk (when the described probabilities are accurate)—imply an initial overweighting of rare events in decisions under risk. Yet, experience eliminates this bias, and the tendency to rely on small samples can lead to the opposite bias. Other likely contributors to the differences between the basic properties of decisions from experience and the predictions of prospect theory are presented shortly. The white bear effect and the weighting of rare events. Wegner et al. (1987) note that when we try not to think about a white bear, a white bear comes to mind. This “white bear effect” can be one of the contributors to the tendency to overweight rare events in decisions from description. For example, it is possible that the gamble 5,000 with probability 1/1,000, and 0 otherwise seems attractive because we cannot avoid paying too much attention to the outcome 5,000 (see Birnbaum and Martin 2003). Underweighting of rare events in decisions from experience emerges, under this logic, because the availability of feedback reduces the attention given to the description and leads subjects to focus on the experienced outcome (Erev, Glozman, and Hertwig 2008). Contingent loss aversion. The loss aversion assertion, one of the cornerstones of prospect theory (Kahneman and Tversky 1979), states that losses loom larger then gains. Thus, it predicts that when selecting among mixed prospects (prospects that can yield both gains and losses), people often prefer the safer prospect over riskier ones with higher expected value. The simplified investment problem examined in Section 1.1.2 reveals the opposite bias: a tendency to prefer the risky prospect even though the safe option provides higher expected return. One explanation of this deviation from loss aversion is that it reflects a simple “experience-description gap” in the reaction to losses. This explanation is plausible, but it has two shortcomings. First, there are many situations in which people do not exhibit loss aversion in decisions from description (see Battalio, Kagel, and Jiranyakul (1990). Ert and Erev (2007, 2013), and the first trial in the simplified investment problem in Section 1.1.2). Most importantly, people appear to exhibit equal sensitivity to gains and losses in decisions from descriptions when the payoff magnitude is low. Thus, it is possible that small losses have a similar effect on decisions from experience and from description. And, the typical behavior in both cases reflects less loss aversion than implied by prospect theory (the predictions of prospect theory do not depend on the payoff magnitude). A second shortcoming of the assumed experience-description gap in the reaction to losses is the observation that certain presentations of the outcomes can lead to behavior that appears to reflect loss aversion in decisions from experience (see Thaler et al. (1997) and a clarification in Erev, Ert, and Yechiam (2008)). For example, when people are

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asked to select between a “sure gain” or a risky prospect that provides higher expected return but often leads to a loss, they exhibit loss aversion when the payoffs are presented graphically (Thaler et al. 1997) but not when they are presented with clear numbers (Erev, Ert, and Yechiam 2008). 1.2 The Effect of Limited Feedback Many natural decisions from experience problems involve situations in which the feedback is limited to the obtained payoffs. For example, when we choose to order a certain dish in a restaurant, we are not likely to know the outcome of ordering a different dish. The current section explores these decision problems with a focus on experiments that use the clicking paradigm (Figure 10.1) with limited feedback. That is, the feedback provided after each trial is limited to the outcome of the selected key. Experimental studies that examine this set of limited-feedback situations highlight the generality of the six phenomena listed before. Yet, the results also demonstrate that the nature of the feedback can change the magnitude of the basic phenomena. The main changes can be described as reflections of the hot stove effect described next. 1.2.1 THE HOT STOVE EFFECT Mark Twain (1897) asserts that after sitting on a hot stove lid, a cat is likely to avoid sitting on stove lids even when they are cold. Denrell and March (2001; also see Denrell (2005, 2007) and a related observation in Einhorn and Hogarth (1978)) show that Twain’s assertion is a likely consequence of learning when the feedback is limited to the obtained payoff. Learning in this setting increases risk aversion. This observation, referred to as the hot stove effect, is a logical consequence of the inherent asymmetry between the effect of good and bad experiences. Good outcomes increase the probability that a choice will be repeated and for that reason facilitate the collection of additional information concerning the value of the alternative that has yielded the good outcome. Bad outcomes reduce the probability that the choice will be repeated and for that reason impair the collection of additional information concerning the value of the alternative that has yielded the bad outcome. As a result, the effect of bad outcomes is stronger (lasts longer) than the effect of good outcomes. Since options with a high variability are more likely to produce bad outcomes, the hot stove hypothesis predicts a decreasing tendency to choose such options. One indication of the descriptive value of the hot stove effect is provided by a comparison of choice behavior with and without foregone payoffs in the fouralternative Iowa gambling task discussed earlier. The availability of foregone payoffs tends to increase risk taking (see Yechiam and Busemeyer 2006). A similar pattern was documented by Fujikawa (2009) in an analysis of problem 9. His analysis suggests that the hot stove effect can reduce underweighting of unattractive rare events. Additional experimental studies demonstrate that the magnitude of the hot stove effect is maximal when the risky alternative is a long-shot gamble. Table 10.2 illustrates this pattern. It presents the proportion of R choices in 12 problems that were run for 100 trials using the basic clicking paradigm (with complete feedback), with and without forgone payoffs (the limited feedback conditions were run by Erev et al. (2010a), and the complete feedback conditions were run by Nevo and Erev (2012)). The results (presented in two blocks of 50 trials) reveal a large hot stove effect in “rare treasure” problems, when the probability of a high payoff from risky choice is 0.1 or lower: In all seven problems of this type, choice of the risky alternative in the last block is higher in

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Block

Complete

Partial

Difference

14

S 7 with certainty R (16.5, 0.01; 6.9)

1 2

0.45 0.46

0.21 0.15

0.24 0.31

15

S −9.4 with certainty R (−2, 0.05; −10.4)

1 2

0.27 0.25

0.16 0.07

0.11 0.18

16

S −4.1 with certainty R (1.3, 0.05; −4.3)

1 2

0.51 0.58

0.31 0.29

0.20 0.29

17

S −18.7 with certainty R (−7.1, 0.07; −19.6)

1 2

0.37 0.39

0.35 0.33

0.02 0.06

18

S −7.9 with certainty R (5, 0.08; −9.1)

1 2

0.41 0.49

0.24 0.14

0.17 0.35

19

S −25.4 with certainty R (−8.9, 0.08; −26.3)

1 2

0.29 0.32

0.11 0.07

0.18 0.25

20

S 11.5 with certainty R (25.7, 0.1; 8.1)

1 2

0.31 0.28

0.12 0.11

0.19 0.17

21

S −15.5 with certainty R (−8.8, 0.6; −19.5)

1 2

0.65 0.71

0.62 0.69

0.03 0.02

22

S 2.2 with certainty R (3, 0.93; −7.2)

1 2

0.48 0.46

0.52 0.35

−0.04 0.11

23

S 25.2 with certainty R (26.5,0.94; 8.3)

1 2

0.54 0.49

0.65 0.42

−0.11 0.07

24

S 6.8 with certainty R (7.3, 0.96; −8.5)

1 2

0.54 0.47

0.70 0.60

−0.16 −0.13

25

S 11 with certainty R (11.4, 0.97; 1.9)

1 2

0.61 0.53

0.69 0.63

−0.08 −0.10

the complete feedback condition. The pattern in the 5 problems with higher probability for the high payoff from risky choice is less clear. Diminishing exploration. As noted before, the hot stove effect is implied by all models that assume positive recency. Explaining the interaction of the observed effect with time and with the magnitude of the high payoff from the risky option is more challenging. The most natural explanation for the effect increasing with time (from the first to the second block) can be captured with the assertion of diminishing exploration: a high exploration rate in the beginning of the experimental session and a lower rate of exploration toward the end. The observation that the hot stove effect was not observed in problems where the risky prospect leads to better outcomes most of the time can be the product of the fact that even limited exploration is enough, in these cases, to demonstrate the value of the risky option. If some exploration continues even after an extreme low payoff, the hot stove effect is not likely to emerge in these settings. Two-armed bandit problems. The task faced by the subjects in the limited feedback conditions of summarized in Table 10.2 is similar to the 2-armed bandit problem (see

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Degroot 1970; Gittins 1989). Yet, the common analyses of 2-armed-bandit problems focus on situations in which the decision makers have more information and the optimal strategy can be computed. Specifically, decision makers know the expected payoff from the safe option and know that the risky option provides one of two outcomes with fixed probability. Theoretical analysis of these 2-armed-bandit problems shows that the optimal strategy is to start with exploration of the risky option and switch to the safe option if the outcome fall below a certain cutoff. Thus, the diminishing exploration pattern suggested here is similar to the optimal strategy in these simpler problems. Direct experimental studies of 2-armed-bandit problems show the robustness of the pattern discussed earlier. Meyer and Shi (1995) show an increase in counterproductive exploration with payoff variability and a slow reduction in exploration (not enough exploration in the beginning and too much exploration in the end). Gans, Knox, and Croson’s (2007) results suggest large individual differences and a “very recent” effect. 1.2.2 I-SAW WITH DIMINISHING EXPLORATION Erev, Ert, and Yechiam (2008) show that the main properties of binary decisions from experience with limited feedback can be captured with an “exploration sampler” model that assumes reliance on small samples and diminishing exploration. The main assumptions of this model can be captured in an extension of I-SAW (Section 1.1.7) that adds the assumption that the probability of exploration depends on the available feedback. I-SAW assumes that when the feedback is complete (includes information concerning obtained and forgone payoff), the probability of exploration is fixed during the experiment and reflect an individual trait (εi ). The extended version adds the assumption that when the feedback is limited to the obtained payoff, the probability of exploration starts at 1 and diminishes with time. The speed of the decline in exploration is assumed to depend on the expected length of the experiment. Specifically, we assume (t−1)/T , where T is that in this case the probability of exploration at trial t equals εi the length of the experiment (in the experiments reviewed in Table 10.2, T = 100). In addition, the extension of I-SAW to situations with limited feedback implies that less information is used during sampling and during the computation of surprise outcomes: only the obtained payoffs are used. 1.3 Two Choice-Prediction Competitions We believe that the basic learning phenomena just considered are an important part of the factors that shape human behavior. This optimistic belief implies that good models of the joint effect of these phenomena can provide useful ex ante predictions of the effect of economic incentives in a wide set of situations (Erev and Roth 1998). Two choice-prediction competitions that evaluate this optimistic hypothesis and facilitate the comparison of alternative learning models are described below. 1.3.1 THE TECHNION PREDICTION TOURNAMENT: INDIVIDUAL DECISIONS WITH LIMITED FEEDBACK Erev et al. (2010a) present a choice-prediction competition designed to facilitate the development and comparison of models of decisions from experience under limited feedback.8 The organizers of the competition (the first three coauthors of that paper) ran two large experimental studies using the clicking paradigm without information concerning forgone payoffs. Each study focused on 60 randomly selected problems. All

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the problems involved a choice between a safe prospect that provides a medium payoff (referred to as M) with certainty and a risky prospect that yields a high payoff (H) with probability Ph and a low payoff (L) otherwise. Thus, the basic choice problem is: S: M with certainty R: H with probability Ph; L otherwise (with probability 1 − Ph) The four parameters (M, H, Ph, and L) were randomly selected with a well-defined algorithm that implies (1) the possible payoffs were between −30 and +30 shekels (1 shekel equaled about $0.30); (2) L < H; (3) M was between L and H in 95% of the problems; and (4) the difference between the expected values of the two prospects was relatively small. Twelve of the 120 problems that were examined are presented in Table 10.2. The first study, referred to as the estimation experiment, was run in March 2008. Each of the 60 problems was faced by 20 subjects for 100 trials. Each subject played 12 games, and the payoffs (in shekels) were determined by a randomly selected trial. In April 2008, the organizers posted the results and the best baseline models that they could find on the Web (see http://tx.technion.ac.il/∼erev/Comp/Comp.html) and challenged other researchers to predict the results of the second study. The second study, referred to as the competition experiment, was run in May 2008 using the same experimental method as the estimation experiment but different randomly selected problems and different subjects. The results of the competition study were not revealed until September 2, 2008. Researchers participating in the competitions were allowed to study the results of the estimation study. Their goal was to develop a model that would predict the results (the mean choice proportion over all choices in each problem) of the competition study. The model had to be implemented in a computer program that reads the payoff distributions of the relevant gambles as an input and predicts the proportion of risky choices as an output. The submission deadline was September 1, 2008. The submitted models were ranked based on the mean squared deviation (MSD) between the predicted and the observed choice proportions. ENO (equivalent number of observations). One advantage of the MSD criteria used here is its relationship to traditional statistics (like regression, t-test and the d-statistic) and its intuitive interpretation. These attractive features are clarified with the computation of the ENO (equivalent number of observations) order-maintaining transformation of the MSD scores (see Erev et al. 2007). The ENO of a model is an estimation of the size of the experiment that has to be run to obtain predictions that are more accurate than the model’s prediction. For example, if a model’s prediction of the probability of risky choices in a particular problem has an ENO of 10, this prediction is expected to be as accurate as the prediction based on the observed proportion of risky choices in an experimental study of that problem with 10 participants. Results. The models evaluated in the competition can be classified in two main classes: the first includes instance-based models like I-SAW that assume that the agents remember specific experiences (and tend to rely on small samples). The second includes models that do not assume memory of and/or reliance on specific experiences. About half of the baseline models and half of the submissions belong to each class. The results reveal a large advantage of the instance-based models. The best baseline model was a predecessor of I-SAW. The ENO of this best baseline was 47.2. In the current context, the predictions of this model are almost identical to the predictions of the refined model, I-SAW, with the parameters εi ∼ U [0, 0.20], wi ∼ U [0, 1], ρi ∼ U [0, 0.6], πi ∼ U [0, 0.6], and μi drawn from integers 1 to 14.9

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The winner of the competition was an instance-based model that assumes an ACT-R cognitive architecture.10 Like the best baseline and I-SAW, the winning model builds on the instance-based learning model proposed by Gonzalez, Lerch, and Lebiere (2003) and implies reliance on small samples from experience. The winner had slightly lower ENO (32.5) than the best baseline model (the baseline models did not participate in the competition), with two attractive features. First, the ACT-R cognitive architecture involves a psychologically more realistic abstraction of the relevant memory processes. For example, it assumes a continuous weighting of all past experiences. Second, the winning ACT-R model is rather general; it was designed to capture decisions in static as well as dynamic environments. We return to this point later. Analysis of the predictions of the models in the competition that do not assume memory of specific experience suggests that their most important failure involves the effect of Ph (the probability of high payoff from risky choice). With the parameters that best fit the data, these models underpredict the R-rate (risk taking). That is, these models overpredict the hot stove effect. This pattern results from extremely low payoffs from the risky prospect decreasing the probability of exploring that prospect. Recent research (Shteingart, Neiman, and Loewenstein 2013) shows that this shortcoming of reinforcement-learning models that do not store specific instances can be addressed by assuming oversensitivity to the very first experience. Their model implies reliance on a very small sample, without explicit memory of this experience. Another outcome from the competition involves the estimation technique: all the leading submissions used a computer-simulation-based estimation method and did not use more sophisticated, one-period-ahead, econometric techniques. This is surprising, as previous research shows that when the model is “well-specified,” the correct oneperiod estimation provides the best estimate of the parameters. One explanation for this is that current models are misspecified, and the one-period-ahead techniques are more sensitive to this misspecification (see Erev and Haruvy 2005). 1.3.2 THE MARKET ENTRY GAME COMPETITION: SOCIAL INTERACTION WITH COMPLETE FEEDBACK Erev et al. (2010b) organized a choice prediction competition that focuses on 4-person market entry games under limited prior information. The experimental subjects were informed that they would play a market-entry game and have to select between a risky entry to the market and a safer decision to stay out of the market. The payoffs depended on a realization of a binary gamble (the realization at trial t is denoted G t , and yields H with probability Ph; and L otherwise), the number of entrants (E ), and two additional parameters (k and S). The exact payoff for player i at trial t was  Vi (t) =

10 − k(E ) + G t if i enters round(G t /S) with p = 0.5; −round(G t /S) otherwise if i does not enter

The parameters H, Ph, L, k and S were randomly drawn under certain constraints (e.g., the expected value of the gamble was zero and the mean entry rate at equilibrium was 0.5). The participants did not receive a description of the payoff rule and had to rely on complete feedback (obtained and forgone payoffs) after each trial. The organizers ran an estimation study with 40 games and a competition study with 40 additional games.

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The results of the estimation study were published in May 2010, and the submission deadline was September 2010. Analysis of the estimation study showed that the results exhibit the basic learning phenomena documented in the individual choice tasks summarized in Section 1.1. In addition, the result shows a high initial entry rate: 66% in the first trial. Comparison of several baseline models highlights the advantage of I-SAW over other models. Best fit was provided with a slight modification of the “strategy set simplification assumption”: the best baseline model is I-SAW with the added assumption of an initial tendency to enter the market in 66% of the trials. Twenty-five teams participated in the competition. The submitted models included basic reinforcement learning, neural networks, ACT-R, and I-SAW-like sampling models. The results reveal a large advantage of instance-based models that assume reliance on small samples and surprise-triggers-change. Indeed, all 10 leading submissions belong to this class of models. The winner of the competition (Chen et al. 2011) is a variant of I-SAW that adds the assumption of bounded memory. The runner-up (Gonzalez, Dutt, and Lejarraga 2011) is a refinement of the instance-based learning model proposed by Gonzalez, Lerch, and Lebiere (2003). The ENO of I-SAW (in predicting the average payoff, a statistic that captures the entry rate and implied coordination level) in the last block of 25 trials was 42.2. As in the first competition, traditional “normal error term” reinforcement-learning models that do not assume reliance on specific instances did not do well. It seems that the main reason for their failure involves the coexistence of underweighting of rare events and a relatively weak recency effect. The traditional reinforcement learning models (and similar fictitious play and experience weighted attraction models; Camerer and Ho (1999)) that were evaluated have to assume a strong recency effect in order to capture the observed underweighting of rare events. Another similarity to the first competition involves the estimation techniques used by the best models. All the top submissions used simulation-based methods and avoided more sophisticated one-period-econometrics.

2 DYNAMIC ENVIRONMENTS Many of the early experimental studies of learning focused on the effect of training in one environment (the training phase) on performance in another environment (test phase). Thus, they examined decisions in dynamic environments. Some of the classical results documented in these settings are reviewed next. 2.1 The Partial Reinforcement Extinction Effect and Reinforcement Schedules The partial reinforcement extinction effect (PREE) is one of the best-known phenomena documented in classical behavioral research. The effect implies that under partial reinforcement schedules (where some responses are, randomly, not reinforced), learned behavior is more robust to extinction, in comparison to continuous reinforcement. This effect was first demonstrated in Humphreys’ (1939a) examination of eye blinks in rabbits. Humphreys (1939b) and Grant, Hake, and Hornseth (1951) show PREE in human behavior. These studies focused on “predicting whether a lightbulb will flash or not.” Participants were presented with two lightbulbs. On each trial, the right-hand bulb was blinking, and the participants had to predict whether the left bulb would blink as well.

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The classical experiments included training and extinction phases and compared two conditions: continuous reinforcement and partial reinforcement. The two conditions differ during the training phase: The response yes (i.e., the prediction that the left light bulb would flash) was reinforced on 100% of the trials under continuous reinforcement and in only some of the trials under partial reinforcement. In the extinction phase, yes was never reinforced. The results demonstrated that in the extinction phase, the rate of yes responses decreased faster for the continuous-reinforcement schedule group than for the partial-reinforcement schedule group. However, during training, learning was faster as the reinforcement rate increased. Hochman and Erev (2013) replicated the PREE using the clicking paradigm. One of their studies focused on the following problems: Problem 26—continuous (r = 100, n = 11, FB = complete, 1 point = ¢ 0.25) S R

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The study included two phases, acquisition (the first 100 trials) and extinction (the last 100 trials). During the acquisition phase, one group of participants (the continuous group) played problem 26, and the second group (the partial group) played problem 27. During the extinction stage, option R was dominated: Both groups were faced with problem 28 at this phase. The participants were not informed that the experiment included two phases. The results (cf. Figure 10.5) reveal more R choices in the continuous group during the acquisition phase and the opposite pattern during the extinction phase. Thus, payoff variability slows the initial learning for R choices, but it also slows the extinction of this behavior. Hochman and Erev (2013) show that the PREE pattern they observed can be captured with a variant of I-SAW that adds the assumption that perceived similarity is determined by the sequence of the last 4 outcomes from R. In order to clarify the intuition behind this observation, consider the decision at trial 106 after the payoff sequence 1, 1, 1, 1 from R. The participants in the continuous group saw this pattern only once in the past (at trial 105), and the outcome from R in that case was disappointing (R gave 1, and S paid 8). Thus, they are predicted to select S. In contrast, the participants in the partial group have seen this sequence several times during the first 100 trials, and in some of these cases it was followed by high payoff from R (17); thus, depending on their exact sample, they may choose R.

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2.2 Spontaneous Alternation, the Gambler Fallacy, and Response to Patterns Tolman (1925) observed an interesting violation of the law of effect in a study of rats’ behavior in a T-maze. Upon receiving a reinforcement in a particular arm, rats tend to switch to the other arm of the maze. According to the common explanation of this spontaneous alternation pattern (see the review in Dember and Fowler 1958), it reflects a tendency to respond to the likely sequential dependencies in natural settings. That is, in most environments where rats eat (e.g., storehouses and garbage dumps), food is replenished independently of feeding. Thus, after eating the food in one location, it is typically optimal to move to a different location. More recent studies use a similar argument to explain probability matching (see Estes 1976; Sonsino 1997; Gaissmaier and Schooler 2008) and underweighting of rare events (Plonsky, Teodorescu, and Erev 2015). These phenomena can be a result of an effort to respond to patterns and sequential dependencies in the environment that implies reliance on small samples. When the environment is static and noisy, this effort impairs maximization. When the environment changes in a consistent fashion, however, sensitivity to sequential dependencies can be very useful (e.g., Gonzalez et al. 2003; Sterman 1989). One example of effective adaptation to consistent change is provided by the continuous condition in the PREE studies (e.g., the change from problem 26 to problem 28). Gaissmaier and Schooler show that people can respond to consistent patterns even when the detection of the pattern requires sensitivity to the last 12 outcomes.

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2.3 Negative and Positive Transfer The effect of learning in one task on the performance of a different task is referred to as transfer. Transfer is highly sensitive to the characteristics of the two tasks (see Osgood (1949) and analysis of economic implications in Cooper and Kagel (2003)). Whereas many studies document positive transfer (improved performance on the second task), other studies document no transfer and even negative transfer. Moreover, many studies report both negative and positive transfer in the same setting. One example is provided by the transfer from problem 26 to 28: the initial transfer in this case is negative (less than 50% maximization rate in the first few transfer trials), but the long-term effect is positive (higher maximization rate in problem 28 when it is played after problem 26). One explanation for the existence of positive and negative transfer involves the assertion that people learn cognitive strategies (rather than situation-specific actions). For example, in problem 26 they might learn to prefer “best reply to recent experiences” over “alternation.” This learning leads to negative transfer in the first trials of problem 28 (S-rate below 50%) but to positive transfer after sufficient experience with problem 28 when recent experience implies that S leads to better outcomes. 2.4 The Effect of Delay and Melioration Thorndike (1911) demonstrates that behavior is highly sensitive to the timing of the reinforcement. Delay of the reinforcement slows learning. This tendency implies (see Kagel, Battalio, and Green 1995) that animals behave as if they prefer a smaller immediate reward to a larger delayed reward and that this preference is not consistent with a simple discounting explanation. A clear demonstration of this pattern is provided by Green et al. (1981) in a study that used a variant of the clicking paradigm. Each trial consisted of a 30-second choice period, during which a pigeon was presented with a choice between two keys, followed by an outcome. One key led to a small reward—2 seconds of access to a grain hopper with a delay of x seconds—and the other to a larger reward—6 seconds of access to a grain hopper, with a delay of x + 4 seconds. The time variable x varied from 2 to 28 seconds. The results reveal that when x is low (less than 5 seconds), each bird strongly favored the smaller, more immediate outcome. The nearly exclusive preference for the smaller reward means that the pigeons failed to maximize total food intake. However, as the delay between choice and both outcomes (the time x) increased, preference reversed, with nearly every bird now choosing the larger, more delayed outcome on more than 80% of the trials. That is, with longer delays the pigeons maximized total food intake. Melioration. Herrnstein and his associates (Herrnstein 1988; Herrnstein and Vaughan, 1980; Herrnstein and Mazur 1987; Herrnstein and Prelec 1991) demonstrate that in certain settings the tendency to underweight delayed payoff can lead to a robust deviation from maximization. Specifically, they show that experience can lead decision makers to behave as if they meliorate (maximize immediate payoffs) rather than to maximize long-term expected utilities.11 For a simple demonstration of this regularity using the clicking paradigm, consider the following choice task. Problem 29 (r = 200, n= 20, FB = complete, 1 point = 0.01 shekel) S R

1 with certainty +10 points with p = N(R)/(50 + t); 0 otherwise

[S-rate: 90%]

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Here t is the trial number and N(R) is the number of R choices made by the participant before trial t. It is easy to see that if the experiment is long enough, option R maximizes long term expected payoff. Yet, melioration implies S choices. The data for problem 29 in a 200-trial experiment reveal strong support for the melioration hypothesis. The choice rate of option S (melioration) over the last 100 trials was 90. All 20 subjects chose S on more than 50% of the trials. Herrnstein et al. (1993) show that melioration decreases with clear information concerning the long-term effect of available choices. Thus, the evidence for melioration is best described as indicative of insufficient exploration. 2.5 Models of Learning in Dynamic Settings Gonzalez, Lerch, and Lebiere (2003) show that the main properties of decisions from experience in dynamic settings can be captured with a variant of the ACT-R model (see Anderson and Lebiere 1998) that assumes similarity-based weighting of all relevant experience. Under this model, decision makers are assumed to overweight a small set of experience that occurred in situations that seem most similar to the current setting and give lower weight to other experience. As noted before, this idea was also found to capture behavior in static settings: It is the basis of the instance-based model that won the choice- prediction competition described in Section 1.3.1. A shortcoming of the similarity-based approach is the determination of a similarity function. Different studies appear to support different similarity functions. For example, Gonzalez et al. show an important role for temporal similarity (also see Hochman and Erev (2013) and Section 2.1) and that this is best determined by the sequence of the last four outcomes. Plonsky, Teodorescu, and Erev (2015) suggest that these apparent inconsistencies can be a reflection of the fact that people consider a wide set of similarity functions, and try to select the best function. When the environment is highly dynamic and predictable, the probability of success is high. However, when the environment is noisy, the probability of success is low, and the observed behavior can be approximated by relying on small samples of randomly selected past experience (recall Section 1.1.7). Recent research shows that learning in dynamic setting can also be captured with reinforcement-learning models that include a recognition process that categorizes cues into situations (see Redish et al. 2007). Gershman , Blei, and Niv (2010) refine this observation and show the value of Bayesian inference within a reinforcement-learning model that assumes an unbounded number of latent causes.

3 MULTIPLE ALTERNATIVES AND ADDITIONAL STIMULI Unlike the simple binary-choice clicking experiments reviewed earlier, most natural activities involve learning among multiple alternatives based on multiple sources of information. Even in the road-crossing example, the decision maker can choose between many actions (different ways to cross the road and different alternatives to this behavior) and can use many signals. Experimental studies that explore learning among multiple alternatives and the effect of different signals are reviewed next. 3.1 Successive Approximations, Hill Climbing, and the Neighborhood Effect Skinner (1938) highlights the value of the method of successive approximations (also known as “shaping”) for teaching complex behavior. Shaping is used when the desired behavior is not observed initially. The procedure involves first reinforcing

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some observed behavior only vaguely similar to the one desired. Once that behavior is established, the trainer looks for (reinforces) variations that come a little closer to the desired behavior, and so on. Skinner and his students have been quite successful in teaching simple animals to do some quite extraordinary things. For example, they taught a pigeon to control a missile (Glines 2005). The basic idea behind the method of successive approximations is the assumption that there are many strategies that can be used in an attempt to perform a complex task. That is, the set of feasible strategies is very large. The agent tends to consider strategies similar to the reinforced strategies. As a result, learning does not ensure convergence to the globally optimal strategy. It can lead to a local optimum. The method of successive approximations is effective because it reduces this risk (at least when the trainer has a good understanding of the location of the optimal strategy). A clear demonstration of the tendency to converge to a local optimum is provided by Busemeyer and Myung’s (1988) examination of choice behavior in a multiplealternative resource-allocation task. In each trial the participants were asked to divide limited resources among three issues. Each allocation can be abstracted as a selection of one of many possible allocations (strategies) that can be placed in a triangle (called the simplex). The results reveal that performance is highly sensitive to the location of the different strategies in the simplex. Higher maximization rate was observed when the best strategies were in the same “neighborhood.” Busemeyer and Myung note that this regularity can be captured by a hill-climbing search process. Erev and Barron (2002) replicated this observation in a study that focused on problems 30 and 31 using the clicking paradigm with limited feedback. Both problems involve a choice among the same 400 alternatives. Each alternative is associated with only one outcome. The two problems differ with respect to the location of the 400 alternatives in the 20 ×20 matrix presentation. The top panel in Figure 10.6 shows a three-dimensional summary of the two matrices. It shows that both matrices have two maximum points (a local maximum of 32 and a global maximum of 52). The conversion rate was 0.25¢ per point. In Problem 30 the local maximum (32) had a wide basin of attraction. Problem 31 was created by swapping the location of the two maxima; thus, the global maximum (52) had the wide basin of attraction. The lower panel in Figure 10.6 presents the proportion of maximization under the two conditions. In line with Busemeyer and Myung’s findings, the decision makers were closer to maximization in problem 31 (global maximum with wide basin of attraction) than in problem 30. Since maximization rate seems to depend on the relative location of the global maximum, we refer to this result as the neighborhood effect. Yechiam, Erev, and Gopher (2001) clarify the relationship between convergence to a local optimum and shaping. They show that a minimalistic shaping procedure, the prevention of repeated choice, reduces the tendency to converge to a local maximum in a variant of problem 30. Implications to descriptive models. The attempt to model learning among multiple alternatives given incomplete feedback highlights the importance of the details of the assumed exploration process. Busemeyer and Myung (1988) show that the main features of the exploration process can be captured with a hill-climbing rule. Erev and Barron (2002) and Yechiam, Erev, and Gopher (2001) show the value of modeling hill climbing as one of several cognitive strategies. The model assumes reinforcement learning among these strategies. Rieskamp et al. (2003) highlight the value of a model that assumes a focus on the difference between the current results and the best past experience.

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Analysis of exploration by firms (Levinthal and March 1993; Gavetti and Levinthal 2000) highlights the value of a distinction between two types of exploration: forward looking and backward looking. Teodorescu and Erev (2014a) demonstrate that this distinction can also shed light on individual choice behavior among multiple alternatives using the clicking paradigm. Their results reflect insufficient exploration in “rare treasure problems” (when the common outcome of exploration is disappointing), and overexploration in a rare mines problem (when the common outcome of exploration is attractive). The coexistence of under- and overexploration can be captured with an extension of I-SAW that assumes a choice between cognitive strategies (exploration or exploration) before the choice between the actions. 3.2 Learned Helplessness Overmier and Seligman (1967) found that dogs exposed to inescapable shocks in one situation later failed to learn to escape shock in a different situation where escape was possible. Follow-up research (see the review in Maier and Seligman 1976) shows that this “learned helplessness” phenomenon is robust across species and experimental paradigms and provides an insightful account of human depression. Teodorescu and Erev (2014b) replicated the learned helplessness pattern in the clicking paradigm and compared three explanations for the results. The three explanations differ with respect to the assumed cause for the tendency to give up too early (and exhibit insufficient exploration). The trigger can be (1) the belief that environment is

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uncontrollable, (2) low average reinforcement from exploration, and (3) low probability of success. The results favor the third explanation. 3.3 Multiple Alternatives with Complete Feedback An increase in the number of possible alternatives increases the importance of the availability of information concerning the forgone payoffs. When the payoff variability is low, the availability of complete feedback facilitates maximization and leads to very quick learning to prefer to the best option (Grosskopf et al. 2006). However, when the payoff variability is large, the availability of complete feedback can lead to the big eyes effect (see Section 1.1.2) that can impair maximization. Ert and Erev (2007) examined a 50-alternative problem (using the clicking paradigm with complete feedback that included the payoff from all 50 alternatives after each choice) in which the predictions of the big eyes effect contradict the predictions of underweighting of rare events. Half of the 50 alternatives provided 3 with certainty, and the other half provided 32 in 10% of the trials and 0 otherwise. Thus, the risky option maximized expected value, and the big eye effect implies risky choice (because the best outcome over the 50 alternatives tends to be 32 from one of the risky alternatives). The choice rate of the risky option (after 50 trials) was only 40%. It seems that in the current setting, underweighting of rare events is stronger than the big eyes effect. This pattern can be captured with the assertion that regret reduces payoff sensitivity. Another explanation assumes limited attention. Specifically, it is reasonable to assume that when the number of alternatives is very large, people cannot attend to all the forgone payoffs (see a related idea in Camerer and Ho 1999). 3.4 The Effect of Additional Stimuli (Beyond Clicking) The current review focuses on the direct effects of obtained and forgone payoffs on choice behavior. We believe that these effects are the most important drivers of human adjustment to economic incentives. Yet, in certain settings other factors can affect this adjustment process. Two important examples are discussed next. 3.4.1 PAVLOVIAN (CLASSICAL) CONDITIONING The early psychological study of learning distinguishes between two classes of basic processes: instrumental and Pavlovian conditioning. Instrumental conditioning (also known as operant conditioning) describes behavior in situations in which the agent learns to prefer specific voluntary actions that affect the environment. Thus, all the studies summarized earlier are examples of instrumental conditioning. The early definition of Pavlovian conditioning focuses on the association between two stimuli. For example, in each trial of Pavlov’s (1927) classical study, dogs were presented with a bell a few seconds before receiving food. At the beginning of the study, the bell elicited no response, and the food elicited salivation (unconditioned response, UR). After several trials the dogs started salivating immediately after hearing the bell. Thus, the bell is called a conditioned stimulus (CS), and the food is called an unconditioned stimulus (US). At first glance Pavlovian conditioning does not appear to be very important in the analysis of economic behavior. However, Rescorla and Solomon (1967) show that more careful analysis can lead to different conclusions: Since Pavlovian conditioning determines emotion and related innate states, it is natural to assume that it affects the

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subjective interpretation of the choice environment. Rescorla and Solomon (see related ideas in Mowrer 1947) propose a two-process model that captures this idea. Under this model, instrumental conditioning drives learning in each subjective state, but Pavlovian conditioning determines the subjective state. Since agents are likely to learn different behavior in different subjective states, Pavlovian conditioning can be highly important. One example of the importance of the subjective states is provided by the dynamic task considered in Section 2, in which the payoff rule changed between the first 100 trials and the last 100 trials (i.e., the payoff rule changed from problem 26 to problem 28) without the subjects being instructed of this two-phase structure. In this setting, distinguishing between the different objective states of the world enhances performance. Thus, if Pavlovian conditioning determines the agent’s responsiveness to these and similar states, it determines in part the learning process. It is interesting to note that Rescorla and Solomon’s theory implies a very different effect of emotions than the common abstraction in economic models of emotion. Under the common abstraction (e.g., Fehr and Schmidt 1999; Bolton and Ockenfels 2000), emotions like inequality aversion affect subjective utility. For example, people reject unfair offers in the ultimatum game because the rejection reduces disutility (negative emotion) from inequality (Fehr and Schmidt 1999; Bolton and Ockenfels 2000). Rascorla and Solomon’s analysis can be used to support the assumption that the main effect of emotion involves the generalization from specific past experiences. In other words, rejection of unfair offers may be a product of an emotion that directs the agent to select a behavior learned in an environment in which rejection of unfair offers is adaptive (see related observations in Cooper and Kagel (Chapter 4). Another example of the economic implications of Pavlovian conditioning involves addiction. Smith and Tasnádi (2007) show that “harmful” addiction can be the result of a mismatch between behavioral (learning) algorithms encoded in the human genome and the expanded menu of choices faced by consumers in the modern world. 3.4.2 OBSERVATIONAL LEARNING Observational learning refers to learning by observing others’ decisions and payoffs. A number of animal studies support observational learning. Terkel (1996) shows that young rats learn to skin pinecones by observing their mothers. John et al. (1969) show that cats can learn tasks by observing the performance of an animal already trained in that particular task. Miller and Dollard (1941) argued that observational learning is no different than simple reinforcement learning in that observational learning involves situations where the stimulus is the behavior of another person and the payoff maximizing behavior happens to be a similar behavior. In one of their experiments, first-grade children were paired, with one in the role of leader and the other in the role of follower. In each trial, the children sequentially entered a room with two boxes. In one of the boxes, there was candy. The leader first chose a box and obtained any candy that was in it. The follower observed which box the leader chose but not the outcome of that choice. Next, the contents of the boxes were emptied and candy was again placed in one box. The placement of the candy was manipulated in two treatments. In one treatment, the candy was placed in the box previously selected by the leader. In the other treatment, candy was placed in the box not chosen by the leader. The follower then entered the room and chose a box. After a few trials, children in the first group always copied the response of the leader and children in the second group made the opposite response.

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Bandura (1965) argued that the payoff received by the observed person should matter in the decision of whether to imitate that person. In Bandura, a group of 4-year-old children watched a short film on a TV screen in which an adult exhibited aggressive behavior toward an inflated “bobo doll.” The children then saw the aggressor being reinforced by another adult. In one treatment, the aggressor was praised and given soda and snacks. In a different treatment, the adult was scolded, spanked, and warned not to do it again. The children were then left in a room with the doll, along with other toys. The imitation and aggression were more pronounced when the adult was observed receiving a reward for his actions and less pronounced when the adult was punished. Merlo and Schotter (2003) raise the prospect that in some settings observational learners may learn better than subjects engaged in the task. In their experiments, subjects chose a number between 0 and 100. The higher the number chosen, the higher the cost incurred by the subject and the higher the probability of winning the high prize, resulting in an interior optimal choice of 37. Subjects in the baseline experiment repeated the decision task 75 times and were paid a small amount after each trial. As each subject performed the experiment, another subject watched over his or her shoulder. In the end of the 75 trials, the observers as well as the active subjects were both given one round of the task with high stakes. The median choice in the high-stakes decisions by the observers was 37 (the optimal choice), whereas the median choice by the subjects who engaged in the small-stakes task was 50. Merlo and Schotter offered this as evidence that the observers learned more effectively than the subjects engaged in the task. Anderson and Holt (1997) studied an interesting situation in which equal weighting of personal information and observational learning (the information obtained by observing others’ actions) leads to an information cascade (that is, it stops the accumulation of knowledge as decision makers stop using their private information). Their results show a lower rate of information cascade than predicted under the rationality assumption. This pattern can be explained by the assumption that people overweight their personal information. Clear support for this assumption is provided by Simonsohn et al. (2008). The participants in their studies received feedback concerning their payoffs (personal experience) and the payoffs of other agents. The results show that the effect of the personal experience was much larger than the effect of others’ experience. Alos-Ferrer and Schlag (2009) review theoretical research that focuses on the value of imitation as a learning strategy. Their analysis demonstrates that payoffs affect the social value of imitation: Efficiency can increase by a tendency to rely on personal information if the advantage of imitation is small.

4 SOCIAL INTERACTIONS AND LEARNING IN GAMES It is constructive to distinguish between two main effects of the social environment on choice behavior. First, the social environment can affect the strategies considered by the decision makers and/or the utility from the obtained payoffs. For example, it can lead the decision makers to consider strategies that facilitate reciprocation, increase fairness, and/or build trust. The second effect is indirect: the social interaction affects the obtained payoffs, and these payoffs shape behavior. Most previous experimental studies of social interactions (games) focus on the direct “reciprocation-related” effects of the social environment (see Cooper and Kagel Chapter 4). The current review tries to complement this research by focusing on the indirect effect of the social environment. It builds on the observation (Roth and Erev

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1995; Erev and Roth 1998) that there is wide set of situations in which the understanding of the obtained payoffs is sufficient to predict the outcome of social interactions. The effect of experience in this space of social situations is similar to the effect of experience in individual choice tasks, and it can be approximated with simple reinforcement learning models like I-SAW. One class of social interactions that belongs to this “basic shaping” space is the class of market-entry games examined in the choice-prediction competition described in Section 1.3.2. The best prediction of the outcome of this class of social interactions was provided by models that capture the basic properties of learning described in Section 1.1. The main goal of the current section is to clarify the boundaries of the basic shaping space. Specifically, it examines the conditions under which the outcome of complex social interactions can be reliably predicted based on simple models that assume learning among the possible alternatives. In addition, it tries to shed light on the assumptions that have to be added to the basic models in order to capture behavior beyond this basic space. Section 4.1 considers studies of learning in games under limited prior information. The results reveal examples of “emerged sophistication” that can be predicted with I-SAW and similar models. Section 4.2 reviews studies of learning in 2-person constant sum games with unique mixed strategy equilibrium. The results reveal that prior information can affect the sequential dependencies in the data but has little effect on the aggregate choice rates. Section 4.3 summarizes studies of cooperation and coordination. The results reveal that under certain conditions, players can learn to maximize efficiency by reciprocating and coordinating. In addition, the results suggest that this “learning-to-reciprocate” phenomenon is rather delicate. It is likely to emerge only when all the following six conditions are met: (1) the agents receive a reliable and complete description of the incentive structure, (2) the benefit from reciprocation is large, (3) the number of interacting agents is small (4 can be too large), (4) the noise level is low, (5) the interaction is expected to continue with high probability, and (6) the framing of the task clarifies the value of reciprocation. These results can be captured with the assertion that players consider “try-to-reciprocate” cognitive strategies. Yet the set of situations under which these strategies can be learned is not large. Section 4.4 discusses studies that explore the role of fairness. The results show that in certain settings people behave as if they try to maximize fairness. However, in other settings they choose actions that reduce equality, even when this action impairs expected return. This pattern can be captured as another indication of considering, but not always using, try-to-reciprocate cognitive strategies. Section 4.5 summarizes the main results and discusses alternative explanations and several open questions. 4.1 Social Interactions Given Limited Prior Information 4.1.1 THE GROUP SIZE EFFECT IN MUTUAL FATE CONTROL GAMES Sidowski, Wykoff, and Tabory (1956; and see Colman 2005; Colman et al. 2010; Delepoulle, Preux, and Darcheville 2000, 2001; Mitropoulos 2001, 2003) studied a minimalistic 2-person social situation in which the players can help each other but cannot affect their own payoffs directly. The top of Figure 10.7 presents a member of this class of “mutual fate” games that was studied in a 200-trial experiment by Colman et al. (2010).

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Figure 10.7: Mutual fate control game (top) and experimental results (bottom): proportions of cooperative choices over four trial blocks in groups of varying sizes. Error bars represent standard errors.

Notice that traditional game-theoretic analysis does not have clear predictions for the current game. Specifically, all 4 cells are weak Nash equilibria points in a 1-shot play of the game.12 The participants in the typical experimental study of this class of games do not receive any information concerning the payoff rule and interact repeatedly in fixed pairs. The results show that most pairs slowly learn to coordinate on the efficient outcome (the “1, 1” cell). The proportion of efficient coordination after 100 trials is close to 70%. Thibaut and Kelley (1959) show that this learning process can be a product of a winstay-lose-shift (WSLS) decision rule. This rule implies a repetition of the last choice after high payoff and a change after a low payoff. Colman et al. (2010) examine the effect of the number of interacting players in a multiplayer generalization of the mutual fate game. In the generalized game the players are placed in a ring, and each player has a predecessor on his or her left and a successor on his or her right. The payoff of each player is determined by her predecessor (the player receives 1 only if his or her predecessor chose C), and the action of each player determines the successor’s payoff. The WSLC rule implies efficient coordination in multiplayer mutual fate games when the number of interacting agents is even (see Coleman, Colman, and Thomas 1990). Colman et al. (2010) experimental results, presented in Figure 10.7, do not support this prediction. Rather, they reflect a large qualitative difference between the basic N = 2 condition and the N > 2 conditions. The players learned to coordinate when N = 2 but

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not when N > 2. A similar group-size effect was documented by Feltovich, Iwasaki, and Oda (2007) in a study of a stag hunt coordination game. Colman et al. (2010) show that this group-size effect can be captured with models that imply a stochastic WSLC decision rule and note that this class of models includes the leading model of decisions from experience in individual choice tasks (like I-SAW) presented in Section 1. 4.1.2 QUICK AND SLOW LEARNING IN MARKET-ENTRY GAMES Erev and Rapoport (1998) document surprisingly fast convergence to Nash equilibrium in 12-person market-entry games that were played without prior information of the payoff rules. In each trial of one of these games participants chose between entering and staying out of the market. Staying out paid a sure payoff of 1. The payoff for entering was 1 + 2(4 − E ), where E is the total number of entrants. This game has multiple pure-strategy equilibria and one symmetric mixed-strategy equilibrium. The average number of entrants at these equilibria is between 3 and 4. The observed number of entrants in trials 15 to 20 (the last block) was 4.1, and the mean obtained payoff was between the expected payoff under the mixed and the pure equilibrium points. At first glance, this coordination appears to contradict the low predictive value of the equilibrium predictions in the market-entry-game competition described in Section 1.3 (the ENO of the equilibrium prediction in this study was below 1). However, there is a simple explanation for the difference between the two studies. Erev and Rapoport examined situations in which the equilibrium prediction implies relatively small differences between the entry rate and the probability that entry is ex-post optimal (the proportion of trials in which entry leads to the best possible outcome). In these situations, learning toward equilibrium is relatively quick. The market entry game competition considered a wide set of games that includes cases with large differences between the equilibrium entry rate and the probability that entry is ex-post optimal. The results reveal that when this difference is large, learning toward equilibrium is slow, and the deviation from equilibrium can be described as reflection of underweighting of rare events. 4.2 Learning in Constant-Sum Games with Unique Mixed-Strategy Equilibrium A two-person constant-sum game is a simplified social interaction that captures pure conflict: the sum of the payoffs of the two players is fixed, and the players cannot reciprocate. The game presented in Figure 10.8 is an example of a constant-sum game with a unique mixed-strategy equilibrium. In this equilibrium player 1 selects A1 with probability p = 3/8 and player 2 selects A2 with probability 78 . Under this mixed strategy, player 2 is expected to receive the same payoff from A2 (EV = 0.7( 38 ) + 0.6( 58 )) and from B2 (EV = 0.2( 38 ) + 0.9( 58 )). Thus, player 2 is not motivated to deviate from his predicted behavior. Similar logic holds for player 1. 4.2.1 SLOW LEARNING AND LIMITED EFFECT OF PRIOR INFORMATION Suppes and Atkinson (1960) examined the game of Figure 10.8 in a 210-trial experiment. The participants were run in fixed pairs: One participant was assigned to be player 1, and the second participant was assigned to be player 2. The payoffs are the winning probabilities. For example, if player 1 selects A1 and player 2 selects A2, then player 1 wins with probability 0.7 and player 2 wins with probability 0.3.

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Two information conditions were compared. The payoff matrix was known to the participants in Condition Known and unknown in Condition Unknown. The feedback after each trial was limited, in both conditions, to the realized outcome (Win or Loss). The results, presented at the top of Figure 10.8, reveal a very small difference between the two conditions. The following observations summarize the results under both conditions: (1) The initial choice rates are close to 50%. (2) With experience player 2 increases the tendency to select A2. That is, Player 2 moves toward the equilibrium prediction. However, this movement is very slow. Even after 200 trials the proportion of A2 choices is closer to 50% than to the equilibrium prediction ( 78 = 87.5%). (3) Player 1 moves away from the equilibrium prediction: The observed proportion of A1 choices was above 60% (in equilibrium, player 1 is expected to select A1 in only 37.5% of the trials). Follow-up research shows the robustness of the pattern documented by Suppes and Atkinson (1960). Slow learning and learning away by one of the players are quite common in constant-sum games with unique mixed-strategy equilibria. Ochs (1995) shows that a similar pattern can be observed in nonconstant-sum games that are played “against a population.” (The experiment was run in cohorts of 8 or more subjects in each role. In each trial all the participants in the role of player 1 played against all the participants in the role of player 2). Erev and Roth (1998; see a clarification in Sarin and Vahid 1999) demonstrate that learning away by one player is predicted by simple models that assume exploitation (selection of the alternative that led to the best outcome in the past) and exploration/error (random choice). I-SAW is an example of this class of models. The right-hand column in Figure 10.8 shows the predictions of I-SAW (with the parameters estimated before) for the current game. Additional indications of the robustness of these results are presented in Table 10.3. This table summarizes the results of experimental studies of three randomly selected constant-sum games. The games were run under two conditions. In Condition Minimal

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Chapter 10 TABLE 10.3: Three of the randomly selected constant-sum games studied by Erev et al. (2002, 2007). The righthand columns present the equilibrium prediction, the observed results, and the predictions of I-SAW. Game (Probability that Player 1 Wins in Each Cell) Statistic

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(see Erev et al. 2002), the participants did not receive a description of the payoff matrix, and the feedback was limited to the obtained payoff. In Condition Complete (see Erev et al. 2007) the participants received a complete description of the payoff matrix and complete feedback. Each game was run for 500 trials under fixed matching. The results show relatively small difference between the two information conditions (the correlation is 0.9), and learning away by one of the players in about half of the games. In addition, the results replicate previous studies (e.g., O’Neill, 1987) that demonstrate a relatively good match between the equilibrium predictions and the observed choice rate when the equilibrium predicts relatively small differences between the choice rates and the proportion of time that the different actions lead to the best payoff. In the context of 2 × 2 games, this condition holds when the equilibrium predictions are close to 50% (e.g., game 3 in Table 10.3). The right-hand column in Table 10.3 presents the predictions of I-SAW (without reestimating the parameters—that is, based on the parameters used in Section 1 to fit the individual choice data) for the complete feedback condition. The MSD score is 0.0047 and the correlation is 0.93. This fit is better than the fit of the best model proposed in the original papers. 4.2.2 SEQUENTIAL DEPENDENCIES It is important to recall that the quick learning toward the mixed-strategy equilibrium predictions, documented when the difference between the predicted choice rate and the implied success rate is relatively small (e.g., game 3 in Table 10.3), does not imply convergence to equilibrium. Studies of games in which aggregate behavior moves toward the equilibrium reveal that the sequential dependencies in the data differ from the predicted dependencies: Brown and Rosenthal (1990) reanalyzed O’Neill’s (1987) results and found strong evidence of serial correlation in players’ choices that contradict the equilibrium prediction (that imply no sequential correlations). The typical subjects exhibit overalternation. A similar overalternation bias was also

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documented by Rapoport and Budescu (1997) in a symmetric 2 × 2 game. Shachat (2002) shows that this deviation from the equilibrium emerges even when the players are allowed to use a randomization device. Additional research suggests that the exact nature of the sequential dependencies in constant sum games is situation specific. For example, evaluation of the sequential dependencies in the constant sum games presented in Table 10.3 reveals that most subjects exhibit the opposite bias: Strong inertia (see Erev et al. 2007). Under one explanation of this pattern, overalternation emerges when the players are informed that they are selecting between objectively identical alternatives. 4.2.3 MODELING ROBUST CHOICE RATES AND SLIPPERY SEQUENTIAL DEPENDENCIES The constant-sum results presented earlier appear to reflect an interesting inconsistency: Section 3.2.1 suggests that the aggregate choice rates can be predicted with the assumption that behavior in different constant-sum games is driven by a general learning model like I-SAW, and Section 3.2.2 suggests situation-specific sequential dependencies. One resolution of this apparent inconsistency is based on the assumption that the different sequential dependency patterns are reflections of different situations- and person-specific exploration patterns that have limited effect on the aggregate choice rate (see a similar idea in Rapoport et al. 1997). This resolution can be naturally incorporated in a variant of I-SAW that allows for the possibility that during exploration, the agents tend to alternate between alternatives that are known to be similar. 4.3 Cooperation, Coordination, and Reciprocation Rapoport, Guyer, and Gordon (1976) show that under certain conditions people can learn to cooperate in public good games and can learn to achieve efficient coordination. A clear demonstration of the emergence of cooperation is provided by the study of the prisoner’s dilemma game presented in Figure 10.9 (Game PD1). Each player in this 2-person normal-form game has to select between cooperation (C) and defection (D). When the game is played once, D is a dominant strategy (and the unique Nash equilibrium of the game). That is, each player earns more from selecting D than from C, independently of the choice of the other player. Yet, both players earn less when both select D (payoff of −1) than when they select C (payoff of 1). In one of the experimental conditions, the participants played game PD1 for 300 trials against the same opponent (fixed matching) with immediate feedback after each trial (and without knowing how many trials would be played). The results (upper panel in Figure 10.9) show an increase in cooperation with experience. The cooperation rate in the last block was higher than 60%. A clear indication of the emergence of coordination is provided by Rapoport, Guyer, and Gordon’s (1976) study of following chicken game: Game: Chicken 1 Swerve Drive

Swerve 1, 1 10, −1

Drive −1, 10 −10, −10

Notice that the game has two pure-strategy equilibria and one mixed-strategy equilibrium. The pure-strategy equilibria (swerve, drive and drive, swerve) are efficient (joint payoffs of 9) but unfair (one player wins 10 and the other loses 1). At the

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symmetric mixed-strategy equilibrium, both players drive with probability 12 , and the expected payoff is 0. The results reveal that participants were able to achieve a high level of cooperation through alternating between plays of the game as to which player would drive and which would swerve. The efficient outcome (joint payoff of 9) was obtained in 84% of the trials. In addition, the results reveal a high level of fairness. The difference between the proportions of driving choices was lower than 7% for all 10 pairs. Alternating behavior that facilitates efficiency and fairness was also shown by Arifovic, McKelvey, and Pevnitskaya (2006). They show that subjects playing repeated Battle of the Sexes, where there are two pure-strategy Nash equilibria, each favoring one player, often fall into a stable pattern of alternation between the two pure strategies. The data provided on the Web site accompanying the article shows that, out of 16 subjects matched in 8 fixed pairs, 56% individually alternated beginning in period 2. This is the proportion of subjects who chose a different action in period 2 than in period 1. By period 3, this proportion rose to 88% and by period 6, it reached 94%, which is all but one of the 16 subjects. The emergence of cooperation and alternation-based coordination described here cannot be captured with basic reinforcement learning models like I-SAW. In the current context, human agents exhibit higher social intelligence and/or sensitivity than assumed by the basic learning models. In order to clarify the implications of this observation, the following sections review studies that highlight the conditions that facilitate sophisticated cooperation and coordination The effect of the relative benefit from reciprocation. Rapoport and Chammah (1965) compare game PD1 with six other prisoner’s dilemma games (same qualitative relationship between the different payoffs). Their results reveal high sensitivity to the relative

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benefit from cooperation. For example, when the benefit from unilateral defection was increased from 10 to 50, the cooperation rate decreased to 27%. Size matters. The increase in cooperation with experience, discussed here, tends to weaken and even disappear as the number of interacting subjects gets large (e.g., Isaac and Walker 1988; Andreoni and Miller 1993; Daniely 2000; Huck, Normann, and Oechssler 2003; Bereby-Meyer and Roth 2006; Apesteguia 2006). That is, the likelihood of learning to cooperate is highly sensitive to the number of interacting agents. An increase in the number of interacting agents tends to increase the tendency to select the dominant strategy. A similar pattern was documented in the study of coordination games (Van Huyck et al. 1990; Bornstein, Budescu, and Zamir 1997). For example, Daniely (2000) compared two versions of Rapoport and Chammah’s prisoner’s dilemma experiment (using game PD1). The first, referred to as “fixed matching,” was a computerized replication of the original study. The participants were run in cohorts of 4 that were divided into 2 pairs. Each pair interacted 300 times. The results of this condition were very similar to the original results. The proportion of cooperation in the last block of 50 trials was 80%. The second condition, referred to as “random matching” (cf. Figure 10.9), was identical to the first, with the exception that the 4 participants in each cohort were randomly rematched after each trial. That is, the set of interacting agents over the 300 trials was increased from 2 to 4 (but the set of interacting agents in each trial was only 2 in both conditions). This change had a dramatic effect on the results. The proportion of cooperation in the last block of 50 trials dropped to 10%. Apesteguia (2006) examined a 6-person public good game with and without description of the payoff rule. The results reveal very similar pattern in the two conditions. Another source of support to the suggestion that reciprocation is highly sensitive to the increase from 2 to 4 players is provided by Isaac and Walker (1988). They examined public good games (which can be described as generalized multiplayer prisoner’s dilemma games). Their results showed a low cooperation rate in 4-player groups and similar rates with 7 agents (when the cost of cooperation is fixed). Isaac, Walker, and Williams (1994) highlight an interesting boundary condition to the negative effect of group size on cooperation. Their results show that when an increase in group size increases the probability of very high payoffs from cooperation, it can eliminate the typical decrease in cooperation over time. The role of framing. In addition to the two conditions described previously, Daniely (2000) studied the effect of framing. She tried to replicate the fixed matching study of game PD1 with the framing of the task as a transportation problem. Each player controlled a simulated car that approached a traffic light and had to decide between staying in his or her lane and changing lanes. The decision to change lanes increased the player’s payoff and decreased the payoff of the other player. The exact payoff rule was determined by game PD1, with change implying D and stay implying C. As in the original study, the participant received a complete description of the payoff rule, and the feedback after each trial was complete. The only change between the studies was the addition of the transportation cover story. The results reveal that this addition eliminated the increase in cooperation. The observed cooperation rate in the last block of 50 trials was only 18%. Additional indications for the significance of the framing effect in the context of social interactions are presented by Rottenstreich (1995). The shadow of the future. Selten and Stoecker (1986) studied behavior in a sequence of prisoner’s dilemma games. Each player played 25 supergames, where each supergame consisted of a 10-round play of game PD2 (first panel in Table 10.4). Following each

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PD5: Dal Bó and Fréchette

supergame, each player was rematched to a new opponent. The typical outcome was initial periods of mutual cooperation, followed by an initial defection, followed by noncooperation in the remaining periods. That is, the understanding that the game is about to end—or the lack of shadow cast by the future (Dal Bó 200513 )—decreases endgame cooperation with experience. While early game cooperation increases with experience, so does endgame defection. Moreover, the first period of defection occurs earlier and earlier in subsequent supergames. Selten and Stoecker note that this learning pattern can be captured with a simple direction-learning model. Andreoni and Miller (1993) studied game PD3 (second panel in Table 10.4) using the Selten and Stoeker prisoner’s dilemma design. Their results replicated both the increase in early-round cooperation and the increase in late-game defection with experience between supergames documented by Selten and Stoeker. However, unlike Selten and Stoeker’s finding that the defection period occurs earlier with experience, they find that the defection period occurs later with experience. The difference between the two studies could be attributed to the weaker temptation to defect in Andreoni and Miller’s matrix. This interpretation of the results is consistent with findings by Dal Bó and Fréchette (2011) in the infinitely repeated PD games. Kagel and McGee (forthcoming), who studied finitely repeated PD supergames under the same paradigm—with individuals as well as teams—found that one factor determining whether subjects will defect earlier or later is the behavior of the partner. When the partner defected first in the previous supergame, subjects tended to defect earlier in the subsequent supergame. In essence, subjects are reacting to the past. Noise matters. Bereby-Meyer and Roth (2006) examined the effect of payoff variability on choice behavior in a prisoner’s dilemma game under Selten and Stoeker’s supergame paradigm and under random matching. They focused on game PD4 (lower panel in Table 10.4). In the stochastic condition, the matrix entries represent the probability of winning $1. In the deterministic condition, the entries represent payoffs in cents. The results reveal an interesting interaction. Payoff variability increased cooperation given random matching but impaired cooperation under repeated play. The effect of prior information. Coordination and reciprocation becomes very difficult when the agents do not know the incentive structure. As noted in Section 4.1, when

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the information is limited, coordination is difficult even in a common-interest game (Colman et al. 2010). 4.3.1 ALTERNATIVE ABSTRACTIONS: SOCIAL UTILITIES AND COGNITIVE STRATEGIES Previous research highlights the value of the two main approaches capturing the effect of experience on cooperation and coordination. One approach is based on the importance of social utilities. For example, an increase in reciprocation can be captured with the assumption that successful reciprocation is reinforcing (see Macy and Flache 2002. Vega-Redondo 1997; Juvina et al. 2013). One recent demonstration of the potential value of this approach is the observation that people behave as if they find the act of following advice reinforcing (see Biele et al. 2009). A second approach involves the assertion, discussed earlier, that people learn among a subset of repeated game strategies. For example, Erev and Roth (2001) assume that the player considers a “reciprocation” strategy that requires effort to reach the most efficient outcome (and punishes opponents who deviate from this play). When this strategy leads to good outcomes, players learn to select it. In another model (Hanaki et al. 2005), the players are assumed to consider strategies that can be represented by automata having no more than 2 states. Analysis of this model shows that it can capture the emergence of reciprocation. Alternative abstractions of the cognitive strategies idea involves a distinction between learning and teaching (see Camerer, Ho, and Chong 2002; Ehrblatt et al. 2006). Cooperation emerges under these models when sophisticated players are able to teach their opponents that cooperation is beneficial. 4.4 Fairness and Inequity Aversion Studies of decisions from description demonstrate that in certain cases, people try to avoid inequity (increase fairness) even when this effort decreases their payoff (see the review in Cooper and Kagel in Chapter 4). Evaluation of the effect of inequity on learning reveals mixed results: Some studies show strong evidence for inequity aversion, but some studies suggest inequity seeking. One demonstration of the effect of equity on learning is provided by Rapoport et al. in the prisoner’s dilemma game described in Figure 10.9. Their results show almost perfect correlation between the payoffs of the two agents in each pair. Another indication for inequity aversion is provided by studies of repeated ultimatum games (Guth, Schmittberger, and Schwarze 1982). In the basic version of this game, one player—the proposer—proposes a division of a pie (e.g., $10 in the experiment considered shortly) between himself or herself and a second player. In the second stage the second player—the responder—can accept or reject the proposal. If he or she accepts, each player gets the proposed share. If he or she rejects, both get nothing. The game-theoretic solution (subgame perfect equilibrium) states that the proposer should offer the smallest possible amount to the receiver, and the receiver should accept it. Abbink et al. (2001) examined a variant of this game in which the proposer’s payoff, in the case of a rejection, was either 0 (as in the original game) or 10. Only the responders were informed of the proposer’s payoff in the case of rejection. Responders were three times more likely to reject the unequal split when doing so enhanced equity (both players got 0) than when it reduced equity (when the rejection payoff to the proposer was 10 and 0 for the responder). Indication for inequity seeking is provided by a study of betting games (Sonsino, Erev, and Gilat 2002; Erev et al. 2015). For example, in one of the conditions in

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Erev et al., two agents have to decide between a participation in a zero sum bet and a safe prospect that implies a fair and efficient outcome (both agents gain 6 units). If both select the bet, one of them pays x units (x = 10, 20, 30 or 40) to the other agent. The game structure implied that rational consideration (and risk aversion and loss aversion) should lead the subjects to prefer the safe, efficient, and fair outcome. Yet the results reveal a high initial betting rate (about 80%) and very slow learning to stop betting. The betting rate after 250 trials with immediate feedback was around 50%. These results can be explained as a reflection of 2 of the regularities discussed earlier: The initial deviation from the fair equilibrium suggests that sensitivity to framing can be more important than inequality aversion, and the slow learning demonstrates the significance of the payoff variability effect. 4.5 Summary and Alternative Approaches The current review of learning in social interactions shows three factors at play. First, learning in games can result in the emergence of reciprocation: in certain situations agents learn to increase their payoff by cooperating and coordinating. Second, the emergence of reciprocation can be captured with the assertion that the agents consider “try-to-reciprocate” cognitive strategies. Strategies of this type drive choice behavior when they are reinforced. Finally, the results suggest that there are many situations in which the effort to reciprocate has little effect on choice behavior. In these cases the effect of the incentive structure can be captured with the basic learning models presented in Section 1.14

5 APPLICATIONS AND THE ECONOMICS OF SMALL DECISIONS The experimental studies reviewed earlier focus on small decisions: The stakes in the typical experimental task were small, and the participants did not invest very much time and/or effort in each choice. Nevertheless, we believe that the behavioral regularities documented in this research can be of high practical value. Our belief is based on three sets of observations. First, many important economic phenomena are the direct product of small decisions. For example, small decisions by drivers (e.g., the choice between the gas pedal and the brake pedal) affect traffic accidents, traffic jams, and pollution. Similarly, small clicking decisions by Internet users determine the future of newspapers and of the music industry. Second, in many settings high-stakes decision problems are shaped by small decisions. For example, consider the high-stake decision among different job offers. In many cases this big decision problem is affected by earlier small decisions. The job offers available to a specific college graduate are likely to depend on small decisions that he or she has made as a child and as a student. Wise small decisions can help obtain high grades and build good social network that increase the probability of good job offers. A third set of observations comes from studies that directly examine and demonstrate the practical implications of the learning phenomena reported on here. Some of these studies are reviewed next. 5.1 The Negative Effect of Punishments The most influential contribution of the experimental analysis of learning is probably Skinner’s (1953) clarification of the negative effects of punishment. Skinner focused

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on an environment in which (benevolent) “teachers” can use both reinforcements and punishments to shape the behavior of “students.” His analysis shows that the overall effect of punishments can be negative even when they appear to be effective in reducing the frequency of the punished behavior. Specifically, the overall effect of punishments depends on the existence of “avoidance options”: behaviors that differ from the shaping goals but can protect the students from punishments. An extreme example is the effect of punishments to facilitate effective reading and writing. When the teacher punishes errors, the student can learn to avoid these punishments by not coming to school. Skinner’s simple observation was among the most important triggers for policies that banned the use of corporal punishments in school. Analysis of the effect of these “less punishment” policies suggests that they are associated with a decrease in school dropouts and crime (Straus 1991). Notice that Skinner’s insight builds on three of the phenomena described before. First is melioration by the students. The tendency to avoid punishment by dropping out of school can be a reflection of insufficient sensitivity to delayed outcomes. A second phenomenon is the hot stove effect, which leads to convergence to a local maximum: Most students who had failed to master reading and writing could master these skills if they would have continued to explore different studying and remembering methods, but they gave up too early. Finally, the teachers’ tendency to punish bad performance can be a reflection of underweighting of rare events (that can be the product of reliance on small samples). From the teacher’s point of view, the common outcome of punishment tends to be positive (the students try harder), and the problematic avoidance reaction is rare. 5.2 The Enforcement of Safety Rules The research reviewed in Sections 1– 4 has six implications for the design of safe working environments (see Erev and Rodensky 2004; Schurr, Rodensky, and Erev 2014; and related ideas in Zohar 1980). First, the results suggest that rule enforcement is necessary even when safe behavior (e.g., the use of safety equipment) is the rational course of action. The explanation of the relevant risks might not be enough. When workers make decisions from experience, they are likely to underweight the low-probability-highhazard event and behave as if they believe it won’t happen to them. A second implication involves the negative effect of punishment, described earlier. Punishment can be an effective enforcement method only when the risk of problematic avoidance behavior is sufficiently low. Two additional implications concern the effectiveness of rule-enforcement systems in which a small proportion of the violations are severely punished (see Becker 1968). The current review implies that systems of this type are likely to be effective in the context of decisions from description, but less effective, or ineffective, in the context of decisions from experience. When decisions are made from experience, low-probability punishments are likely to be underweighted. A related implication comes from studies of the importance of fairness considerations in social interactions, as in the ultimatum game experiments discussed earlier. This research suggests that the implementation of low-probability heavy punishments may be very difficult if the recipient can affect the enforcers (the proposer’s role). Under the assumption that punishment may seem unfair (because only some violators are punished), some recipients are likely to retaliate even if retaliation is costly to them. Thus, enforcers (proposers) might learn to avoid using these punishments.

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Figure 10.10: Percentage of workers who obey the safety rule and use the required safety equipment as a function of time in one of the departments (studied by Schurr, Rodensky, and Erev 2014).

A fifth implication is optimistic. It implies that the fact that workers take unnecessary risks and behave as if they ignore safety rules does not imply that they will object to attempts to enforce these rules. Indeed, the observation that low-probability events are overweighted in decisions from description implies that when workers are explicitly asked to consider the safety issue, they will agree that they want to behave safely and will be happy to see that the management designs a rule-enforcement system to help them achieve this goal. Finally, the arguments just presented suggest that behavior is much more sensitive to the probability than to the magnitude of the punishment. Thus, a gentle continuous punishment (“gentle COP”) policy that implies low punishments with high probability can be very effective (as long as the fine is larger than the benefit from violations of the rule and the risk of avoidance behavior is low). Erev and Rodensky (2004; and see Erev 2007; Schurr, Rodensky, and Erev 2014) applied this gentle COP method in 12 Israeli factories. The basic idea was to design a mechanism by which supervisors will be encouraged to approach each worker who violates the safety rule and remind him or her that this behavior might result in injury and will be recorded (if repeated). The official role of these violations’ records was to allow the management to positively reinforce workers who observe the safety rule by giving these workers a higher probability of winning a lottery. Baseline data were collected about 2 months prior to intervention. The data included objective measures of the workers’ safety behaviors (cf. Figure 10.10). The intervention started with a formal presentation of the new policy to all the workers. Figure 10.10 presents measures of safety related behavior before and after the presentation in one of the departments in one of the twelve factories. The baseline data were collected by the research team a month before the beginning of the intervention (in September 2003) and were independent of the supervisors’ comments and records. As demonstrated in Figure 10.10, the intervention had a large and immediate positive effect. A similar pattern was observed in all 12 factories. The rate of safe behavior

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increased to 90% immediately after the beginning of the intervention. More interesting is the observation that the effect of the intervention did not diminish with time. The rate of safe behavior increased or stayed high during the 2 years since the beginning of the intervention. Given the success of the intervention and its relatively low cost, the factories have decided to maintain the experimental policy.

5.3 Cheating in Exams One of the likely contributors to the long-term success of the gentle COP procedure is the observation that multiple equilibria are common in rule-enforcement problems, including tax compliance (Alm and McKee 2004) and corruption (Tirole 1996; Waller, Verdier, and Gardner 2002). In one equilibrium, obeying the rules is the norm, and the enforcers can easily detect and punish deviations if they occur. Thus, no one is motivated to start violating the rule. In a second equilibrium, violation is the norm, and the enforcers are unable to cope with the frequent violations. The possibility of two extreme equilibria and the hypothesis that small decisions are made based on experience in similar situations implies that the effectiveness of different rule-enforcement policies is likely to be particularly sensitive to the initial actions. Wise allocation of initial resources can lead to a convergence to the “good” equilibrium, in which observing the rule is the norm. Erev, Ingram, et al. (2010) applied this reasoning to cheating on college exams. Their analysis suggests that gentle COP policies can be used to move behavior to the good equilibrium. To evaluate this hypothesis, they ran an experiment during final semester exams of undergraduate courses at the Technion. Traditionally, instructions for exam proctors at the Technion included the following points: 1. The student’s ID should be collected at the beginning of the exam. 2. A map of students’ seating should be prepared.15 Since the collection of the ID is the first step in the construction of the map, the common interpretation of these instructions was that the map should be prepared at the beginning of the exam. Early preparation of the map reflects an attempt to follow Becker’s idea (preparing evidence to facilitate large punishments) but distracts the proctors and reduces the probability of gentle punishment (e.g., warning or moving the suspected student to the first row) at the beginning of the exam. The experiment compared two conditions that differed with respect to the timing of the preparation of the map. In the control condition, the proctors were requested to prepare the map at the beginning of the example (as they did before the study), and in the experimental condition, they were requested to delay the preparation of the map by 50 minutes. Seven undergraduate courses were selected to participate in the study. In all courses the final exam was conducted in two rooms. One room was randomly assigned to the experimental condition, and the second was assigned to the control condition. After finishing the exam, students were asked to complete a brief questionnaire in which they are asked to rate the extent to which students cheated in this exam relative to other exams. The results reveal a large and consistent difference between the two conditions. The perceived level of cheating was lower in the experimental condition in all seven comparisons.

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5.4 Broken Windows Theory, Quality of Life, and Safety Climate In an influential paper, Kelling and Wilson (1982) suggest that physical decay and disorder in a neighborhood can increase the crime rate. This suggestion, known as the broken windows theory, was motivated by a field experiment conducted by Zimbardo (1969). The experiment focused on two cars that were abandoned in the Bronx, New York, and in Palo Alto, California. The results showed that vandalism of the cars started only after the experimenter created disorder (by removal of the license plate or breaking a window). The broken windows theory was a motivation for the “quality-of-life” policing strategy implemented in New York City in the mid-1990s (Kelling and Sousa 2001). This policing strategy advocated increasing the number of police on the streets and arresting persons for less serious but more visible offenses. Some credit this strategy for the decline in crime and disorder (Golub et al. 2002; Kelling and Sousa 2001, Silverman 1999). However, there are other explanations for the decline (see Eck and Maguire 2000). Field studies that test the broken windows hypothesis provide mixed results. Skogan (1990) found that robbery victimization was higher in neighborhoods characterized by disorder, but Harcourt (2001) found that the crime-disorder relationship did not hold for other crimes, including burglary (housebreaking), assault, rape and pickpocketing. We believe that the studies reviewed here can help clarify this mixed pattern. Under the current analysis, quality-of-life policing can be effective for the same reason that gentle COP policies are effective. When the probability of detection is very high and the risk of problematic avoidance behaviors is low, people learn to obey the rule. Thus, quality-of-life policing is effective in reducing robberies because these violations are more likely to be detected by the additional neighborhood police. Luria, Zohar, and Erev (2008) examined this “probability of detection” explanation in the context of a safety-climate intervention (Zohar 1980). Safety-climate interventions are very similar to quality-of-life policing. These interventions are designed to create a safer work climate. This goal is achieved by encouraging supervisors to exhibit commitment to safety (e.g., by measuring the number of times they discuss safety issues with their subordinates). Zohar (1980) and Zohar and Luria (2005) show that this manipulation increases safety. To test the probability of the detection hypothesis, Luria et al. reanalyzed the data reported in Zohar and Luria. Their results show that the safety climate decreases unsafe behavior in environments with high visibility (the supervisor can detect rule violation with high probability) but not when visibility is low. Notice that this explanation for the effect of quality-of-life policing has nontrivial positive and negative implications. On the positive side, this explanation implies that it may not be necessary to arrest all violators of minor crimes. If the probability of detection is high enough, more gentle punishment may be enough. For example, if the probability of detecting an attempt to use public transportation without paying is close to 1, then a fine that is only slightly larger than the regular cost should be sufficient. On the negative side, the current analysis suggests that quality-of-life policing is not likely to succeed when the probability of detection is low. 5.5 Hand Washing Hand washing is a nice example of the difference between decisions from experience and decisions from description. The consequence of a failure to wash one’s hands is

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potentially devastating—including serious illness or even death. The cost of washing one’s hands is a few seconds of inconvenience. Everything we know about decisions from description—including risk aversion, loss aversion, and overweighting of small probabilities—suggests that people would be eager to wash their hands. Yet, repeated experience following not washing one’s hands is likely to result in no noticeable negative outcome and, therefore, in extinction of this desirable behavior. In 1847, Dr. Ignaz Semmelweis first demonstrated that routine hand washing could prevent the spread of disease. In an experiment, Dr. Semmelweis insisted that his students staffing a Vienna hospital’s maternity ward wash their hands before treating the maternity patients—and deaths on the maternity ward fell dramatically. In one case, it fell from 15% to near 0%! Though his findings were published, there was no apparent increase in hand washing by doctors until the discoveries of Louis Pasteur years after Dr. Semmelweis died in a mental asylum (Nuland 2003).16 Moreover, many believe that even today medical professionals do not do enough on this front. In a recent study, Erev, Rodensky, et al. (2010) used a variant of the gentle COP policy, described earlier, to increase the use of gloves by doctors and nurses. They focused on the use of gloves while taking blood and giving infusions in 12 distinct departments. The gentle intervention consisted of a single meeting with the department staff. During this meeting the researchers suggested that the participants help each other remember to use gloves. That is, when they see a friend approach a patient without new gloves, they should ask him or her to fix the problem. The results show that this minimal manipulation increased glove use from 50% to 95%. 5.6 The Effect of the Timing of Warning Signs Evaluation of the impact of warnings reveals a large effect of prior experience (see Barron, Leider, and Stack 2008). Individuals who have had good experiences in the past are less affected by warnings. For example, when the FDA added a black-box warning to the drug Cisapride, the data show an increase in usage of 2% among repeat users, but a decrease of 17% among first-time users (Smalley et. al. 2000). Another example is provided by a study of parent-adolescent sexual communication. Regular condom use was found to be lower when parent-adolescent sexual communication occurred at a later age (Hutchinson 2002) as students had presumably already engaged in unsafe sexual activity and found it pleasant. Barron et al. show that the effect of experience remains even after controlling for the available information. Indeed, experience reduces the tendency to respond to informative warnings even if the experience does not provide additional information. It seems that part of the effect of experience is to underweight warnings as a result of inertia. 5.7 Safety Devices and the Buying-Using Gap The difference between decisions from experience and decisions from description suggests that in certain cases people may buy safety devices but “learn” not to take the necessary measures to benefit from them. One example of this buying-using gap is a study by Yechiam, Erev, and Barron (2006) that focuses on car radios with a detachable panel. The detachable radio panel was (around the end of 20th century) a rather popular example of a safety device (against theft) that can be effective only when it is used (detached). Notice that the main role of a detachable panel to a car radio is its value as a safety device. The decision not to detach the panel is made without explicit presentation of a threat and is likely to be shaped by repeated experience. Thus, the properties of decisions

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from experience imply a decrease in the tendency to use the panel with experience, since the small probability of theft is underweighted. Yechiam et al. found (using a short survey) that the large majority (96%) of Israelis who bought car radios between 1995 and 2003 preferred the type with a removable panel even though it was more expensive. Most participants detached the panel in the first 2 weeks and were much less likely to detach it after a year. That is, responders behaved as if they gave more weight to the probability of theft in their initial-use decisions than in their use decisions after a year of experience. 5.8 The Effect of Rare Terrorist Attacks Previous studies reveal that even rare terrorist attacks can have large negative effects on international tourism. For example, following terrorist activity in Northern Ireland in the early 1970s, visitors fell from close to 1 million in 1967 to about 300,000 in 1976. Yechiam, Barron, and Erev (2005) note that the research just reviewed implies that other effects of terrorism may not be as large. Specifically, it implies a large difference between international and local tourism. Traveling to a different country requires a big decision from description. Local tourism, on the other hand, can be a product of small decisions from experience (e.g., whether to take a sandwich to work or dine in a restaurant) and can be affected by experience. Thus, with experience, the effect of rare terrorist attacks on local residents is likely to decrease. Figure 10.11 presents the number of nights slept in Israeli hotels by local and international tourists before and after the beginning of the wave of terrorist attack that started at September 2000 and lasted several years. The results show a drop for both populations with the beginning of the recent attacks but a quick recovery by local tourists. This trend is consistent with the suggestion that experience reduces the impact of rare attacks.

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Yechiam et al. note that their analysis suggests that the negative effects of rare terrorist attacks (on the economy) can be reduced by ensuring that citizens continue to partake in relatively safe leisure activities. Interestingly, this suggestion summarizes one component of Mayor Rudolph Giuliani’s response to the September 11 attack in New York City. Mayor Giuliani suggested that citizens should invest less in direct contributions (like helping digging and collecting blankets), and spend more time shopping and dining in New York. While this suggestion seemed counterintuitive at the time, the current analysis suggests that it was effective in reducing the negative longterm economic effect of the attack. 5.9 Emphasis-Change Training, Flight School, and Basketball Mane and Donchin (1989) have organized an interesting competition between leading researchers of motor-skills learning. The participants in the competition were asked to develop a training method to improve performance in a complex “space fortress” video game. The human players in this game control a spaceship and try to destroy a space fortress that tries to destroy their ship (using missiles and mines). High performance in this game requires sensitivity to several sources of information (e.g., the location of mines, the movement of missiles, the location of the ship, and the angle of the ship’s gun). One of the most successful submissions to this competition, proposed by Gopher Weil, and Siegel (1989), was based on the idea of emphasis-change training. During training, under this method, the trainees are continuously asked to change their focus. For example, they start by trying to maximize their scores on hitting the fortress, and then they are asked to focus on avoiding mines. The basic idea behind this method is simple: under the assumption that people choose among multiple attention-control strategies, they are likely to converge to a local maximum (see Section 1.3.2). Emphasis change reduces the risk of this problem (see Erev and Gopher 1998) by giving the trainee experience with attention-control strategies he or she might not otherwise sample. The emphasis-change method was a clear winner in transfer tests (see Fabiani et al. 1989). One demonstration of the value of this method is provided by Gopher, Weil, and Bareket (1994). In the experimental group of their study, cadets in flight school were asked to play the space fortress game and practiced using the emphasis-change training method. The results reveal that this experience had a large positive effect on their subsequent performance in flight school. The probability of successful completion of the course increased by 33%. Another demonstration of the value of emphasis-change training is provided by the success of a commercial variant of the space fortress game (see www.intelligym.com) designed to facilitate attention control by basketball players. The commercial product was used by only two NCAA men’s basketball teams in 2005: the University of Memphis and the University of Florida. Florida won the NCAA title in both the 2005–6 and 2006–7 seasons. Twelve NCAA teams used the emphasis change trainer in the 2007–8 season: one of them (University of Kansas) won the title and another user (University of Memphis) was the runner-up. 5.10 The Pat-on-the-Back Paradox Informal rewards, often referred to collectively as pats on the back, are low-cost or no-cost, often verbal, rewards that have virtually no monetary market value. Psychological research has shown that pats on the back can be as motivating as monetary

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awards. For example, Stajkovic and Luthans (1997) present a meta-analysis of 19 studies showing that feedback and social reinforcers may have as strong an impact on performance as monetary rewards. Survey-based data suggest similar conclusions. In a survey of American workers, 63% indicated a pat on the back to be an effective incentive (Lovio-George 1992). In other survey-based studies (Graham and Unruh 1990), paton-the-back incentives are shown to be more effective than monetary rewards. Such findings are often attributed to the recognition bestowed by the pat on the back and have prompted statements such as, “There are two things people want more than sex and money . . . recognition and praise” (Nelson 1994, quoting Mary Kay Ash, founder of Mary Kay Cosmetics). These results appear to be inconsistent with the observation that most job postings focus on the salary, opportunities, and the possibility of promotion and professional development, and not on the likelihood of pats on the back. Luria et al. (2016) show that this “pat-on-the-back paradox” can be resolved as a reflection of the differential weighting on rare events in decisions from experience and from description. This explanation is based on the assumption that the probability of explicit monetary rewards (like promotions and bonuses) in the typical workplace is low. Thus, these events are overweighted when considering a description of the job but are underweighted in decisions from experience. Underweighting of rare rewards is expected to reduce effort in the workplace. To address this problem, wise managers use pats on the back as “lottery tickets” that signal a probabilistic future value (like a possible promotion), thereby reinforcing the behavior in question. 5.11 Gambling and the Medium-Prize Paradox According to the leading explanations of gambling, people gamble because they overweight rare events (Kahneman and Tversky 1979) or because they are risk seekers around the status quo (Friedman and Savage 1948). These factors can explain the popularity of gambling games that promise positively skewed payoff distributions that provide very high payoffs with very low probability. However, they appear to be inconsistent with the observation that a large proportion of the payoffs in many gambling games involve medium prizes. Medium prizes are particularly common in casino settings. Haruvy, Erev, and Sonsino (2001, following Skinner 1953) suggest that the coexistence of high and medium prizes can be a response to two behavioral biases: overweighting of rare events in decisions from description and the payoff variability effect in decisions from experience. High prizes are necessary to attract new gamblers (who respond to a description of the game), and medium prizes are necessary to increase the payoff variability that slows learning (that gambling is costly). 5.12 The Evolution of Social Groups Recent research demonstrates that two of the most basic observations from studies of the development of social groups can be a product of the hot stove effect. Denrell (2005) focuses on the observation that proximity is an important determinant of liking (Brewer and Campbell 1976; Festinger, Schachter, and Back 1950; Segal 1974). Even if students are randomly assigned to rooms, individuals are more likely to become friends with and have a favorable impression of individuals who are nearby (Segal 1974). Denrell’s explanation is simple and elegant: our opinions about our friends are likely to change after each meeting. When these opinions determine the probability of

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future meeting, we will stop meeting a friend when we no longer like him or her (and keep our low opinion). This problem is less severe when the proximity is high. For example, roommates meet independently of changes in their contemporary opinions. Thus, proximity limits the hot stove effect in this setting. Denrell and Le Mens (2007) extend this analysis and show that the hot stove effect can partially explain why friends hold similar beliefs. This observation is based on the assumption that low evaluation of an activity (like eating at a particular restaurant, or attending service at a particular church) decreases the probability of a repetition of this activity. Friendship slows this process because high evaluation by a friend can lead us to repeat activities even when our personal evaluation is low. Another example of a possible effect of decisions from experience to the development of social groups involves the survival of sects and religious groups that demand significant sacrifice. As noted by Berman (2001), successful groups appear to create an incentive structure in which the cost of exiting the group increases over time. Thus, melioration and related properties of decisions from experience can be among the contributors to the success of these groups. 5.13 Product Updating Consumers have long been known to exhibit inertia in moving from one technology standard to another, even when the newer standard is demonstrably superior (Clements 2005; Gourville 2003). Microsoft, for example, the largest and most successful computer software company, is often criticized on the grounds that its products are inferior to competitors’ products. Nevertheless, Microsoft products are often dominant in the market. While the reasons behind Microsoft’s dominance are complicated and numerous (including the importance of establishing a network of users, complementarities, and unfair anticompetitive practices by Microsoft), research on consumption of other experience goods (products that require consumption before knowing their quality) has shown that consumers who behave as hill climbers will be unable to move easily from the old to the new product and will often converge to a local maximum. Consumer learning in experience goods markets has been an important subject of theoretical research in industrial organization and marketing since the 1970s. Learning can be an especially important factor in the demand for new products, and there is an empirical literature that quantifies learning in household panel data for grocery purchases (for example, Erdem and Keane 1996), choice between personal computers (Erdem Keane, and Oncu 2005), and choice between drugs (Crawford and Shum 2005). In these papers, it is assumed that the only type of demand dynamics comes from learning, which creates inertia, partially explaining the reluctance of Microsoft consumers to switch to superior products. Likewise, this explains why many consumers do not immediately switch from a product they currently use to the latest improved product, even if the cost difference is minimal (Gourville 2003). He finds support for the basic learning assumptions described here: consumers are sensitive to relative payoffs of the two products, and their reference points about each product’s quality critically depend on past experience. Local hill climbing can therefore take consumers to a suboptimal product choice and keep them there. 5.14 Unemployment The decision to accept a particular job offer is often not a small decision. The stakes are usually high, and the decision maker is likely to invest time and effort in this choice.

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Nevertheless, many small decisions are likely to affect the employment status of the decision maker. Examples include the decisions to invest effort in particular tasks in school, at work, and while looking for a job. These small decisions are likely to affect the likelihood of receiving attractive job opportunities. Lemieux and MacLeod (2000) present an elegant analysis that demonstrates how the basic properties of learning, reviewed earlier, can shed light on an apparently weak relationship between unemployment rates and public policies. They focus on the unemployment rate in Canada in the period of 1972 through 1992. The Canadian unemployment insurance system greatly increased benefits to the unemployed in 1971. The generosity of the unemployment insurance did not increase again, but unemployment steadily increased from 1972 to 1992. Lemieux and MacLeod note that this pattern can be captured with the assertion that the description of the incentive system has limited effect. The main effect is a result of personal experience with the new incentives. 5.15 Interpersonal Conflicts and the Description-Experience Gap Review of research on interpersonal conflicts reveals an apparent inconsistency between the main conclusions of two major lines of research. On one hand, extensive research in behavioral game theory highlights the importance of other-regarding preferences (see Fehr and Schmidt 1999; Bolton and A Ockenfels 2000; Charness and Rabin 2002; and the review in Cooper and Kagel, Chapter 4). This research suggests that people pay more attention to the incentives of others than predicted under traditional assumptions of fully rational economic man. On the other hand, negotiation research reflects “mythical fixed pie beliefs” (see Bazerman and Neal 1992) that imply the opposite bias: a tendency to ignore the incentives of others and assume that efficient cooperation or coordination is impossible. Erev and Greiner (2015) suggest that this apparent inconsistency can be a product of the difference between decisions from description and decisions from experience discussed earlier. It is possible that social behavior reflects oversensitivity to the outcomes of others when these outcomes are described (the convention in mainstream behavioral economic research) but reflects the basic properties of decisions from experience when the outcomes are not clearly described (the state in most negotiation settings). The basic properties of decisions from experience, in turn, imply a tendency to exhibit insufficient sensitivity to the payoffs of other agents. Erev and Greiner clarify this assertion with the study of the 5 × 5 asymmetric stag hunt game presented in Table 10.5. Notice the game has two equilibrium points: The “E, E” equilibrium is efficient (payoff dominant) and fair: both players win 12 (joint payoff of 24) under this equilibrium. The “A, A” equilibrium is inefficient (joint payoff

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of 15) and unfair (one player wins 10, and the other wins 5), but it is the risk-dominant equilibrium. The game was played repeatedly (for 50 trials), with fixed matching, under 2 information conditions. The participants received a complete description of the matrix in the Description condition but not in the Experience condition. The results reveal a large difference between the two conditions. The modal outcome was efficient and fair (“E, E”—as predicted by other-regarding preferences) in Description condition, and inefficient and unfair (“A, A”—as predicted by the basic properties of decisions from experience) in the Experience condition. The current analysis leads to optimistic predictions: It implies that manipulations that increase exploration (like the emphasis-change procedure described in Section 5.9) can increase social efficiency. This prediction is consistent with the main idea of popular negotiation books. 5.16 Implications for Financial Decisions Typical financial decisions often involve high stakes. Nevertheless, recent research demonstrates interesting similarities between financial decisions and the experimental literature reviewed here. The best-known example is provided by Taleb’s (2007) prediction of the 2008 financial crisis. Taleb used the tendency to underweight rare events in decisions from experience, reviewed earlier, to justify his “black swan” assertion, according to which investors tend to dismiss low-probability events. For that reason, low-probability events, when they occur, can lead to financial crises. Another example involves the assertion that many investors have underdiversified investment portfolios (e.g., Blume and Friend 1975; Kelly 1995). Ben Zion et al. (2010) show that this tendency can be observed in the clicking paradigm and can be a product of the tendency to rely on past experience. A third example concerns sequential dependencies in stock markets. Empirical analyses reveal high correlation between absolute price change in a particular trading day and volume of trade in the following day (see Karpoff 1988). Nevo and Erev (2012) show that this pattern can be a product of the surprise-trigger-change of decisions from experience. 5.17 Summary and the Innovations-Discoveries Gap The first author of the current chapter was recently invited to give a talk in a lecture series with the title “Inventions and discoveries that have shaped the human civilization.” While preparing the talk, he noticed a surprisingly large gap between his favorite examples of inventions and discoveries in economics. Whereas the most influential inventions (e.g., markets, money, banks, rules, credit cards, auctions, e-trading, matching) are based on the assumptions that people try to maximize expected return, many of the interesting discoveries reflect deviations from maximization.17 We believe that the results reviewed here highlight one contributor to this gap. The basic properties of decision from experience imply interesting deviations from maximization but also imply a wide set of situations in which people behave as if they are trying to maximize expected return: When the strategy that maximizes expected return also leads to the best outcome most of the time, people exhibit a high sensitivity to the incentive structure. (This prediction is clarified by I-SAW: when the best alternative is also best most of the time, the “grand mean” and the “sample mean” tend to point in the same direction). It seems that many of the successful economic innovations

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are mechanisms that increase the probability that the socially desired behavior will be reinforced most of the time. Most of the applications considered here follow a similar logic. They start with the discovery of a problematic deviation from maximization that can be the product of the tendency to rely on small samples and then show that the problem can be addressed by a change of the incentive structure that increases the probability that the desired behavior will be reinforced on average—and most of the time.

6 CONCLUSION The research reviewed here can be summarized by six main sets of observations. The first set includes demonstrations of the generality of basic properties of decisions from experience. These behavioral regularities have been observed in animal studies, laboratory studies that focus on the behavior of student subjects engaging in simple tasks, and in the analysis of relatively complex social interactions. An additional indication of the robustness of the main results is provided by the observation that they can be summarized with a simple model (best reply to a small sample of experience in similar situations) that allows for useful ex ante quantitative predictions of behavior in new situations. A second set of observations involves two shortcomings of an approach based on the strictest interpretation of rationality—including equilibrium analysis. First, there are many situations in which this approach leads to ambiguous conclusions (it is “not even wrong”). For example, this approach does not provide a clear prediction of behavior in the clicking paradigm. Almost any behavior can be justified as “rational,” given certain prior beliefs. Second, when the rationality assumption leads to unambiguous predictions, it is often wrong at the intermediate term. For example, learning away from a mixed-strategy equilibria persists for at least 500 trials (see Section 4.2), and learning away from a simulated index fund that is known to maximize expected payoff and minimize variance experience persists for at least 100 trials (see Section 1.3.1). It is important to recall, however, that the current results do not reject the class of “epsilon equilibrium models” (e.g., Radner 1980; McKelvey and Palfrey 1995). Indeed, the descriptive models presented before are members of the class of epsilon equilibrium models: When the incentive structure is strong enough (in the way implied by these models), they imply an approximation of the optimal behavior. A third set involves the conditions under which experience leads decision makers toward maximization of expected return (and risk-neutral equilibrium). High maximization rate was documented when the strategy that maximizes expected return also leads to the best outcome most of the time. Similarly, convergence to mixed-strategy equilibrium was observed when the choice proportions at equilibrium are consistent with the proportions of times in which each alternative leads to the best outcomes. A fourth set of observations concerns the difference between decisions from experience and decisions from description. The results described here suggest that decision makers underweight rare events in decisions from experience but overweight rare events in decisions from description (see Section 1.1.3). Another example of this is the apparent inconsistency between research documenting other-regarding behavior and the finding that some social conflicts reveal the opposite bias (see Section 5.15). The fifth set pertains to the distinction between basic learning properties and other cognitive factors that affect the impact of experience. The current review suggests that

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the effects of other cognitive factors are important but are less general than the basic properties of learning. For example, the indications for learning to follow a reciprocation strategy in a repeated prisoner’s dilemma game are highly sensitive to the framing of the task. Finally, the current review suggests that the study of decisions from experience may shed light on many interesting economic phenomena. Highly consequential economic phenomena may be the result of small and relatively inconsequential decisions by many individuals. The applications presented in Section 5 suggest that experimental research on small decisions can be used to understand larger phenomena and facilitate efficient design of relevant incentive structures.

ACKNOWLEDGMENTS Much of this paper was written when Ido Erev was a Marvin Bower Fellow at Harvard Business School. It was also supported by the I-CORE program of the Planning and Budgeting Committee and the Israel Science Foundation (grant no. 1821/12). We thank Olivier Armantier, Greg Barron, Gary Bolton, Eyal Ert, Dan Friedman, Glenn Harrison, Teck Ho, John Kagel, Elena Katok, Steven M. Kemp, Amnon Rapoport, Al Roth, Andrew Schotter, Uri Simonsohn, Trent Smith, Dale Stahl, Nat Wilcox, and Eldad Yechiam for useful comments.

NOTES 1. “It is unnecessary to assume that the participants have full knowledge of the total structure of the game, or the ability and inclination to go through any complex reasoning process” (Nash 1950, 21) 2. Smith showed that competitive equilibrium could be attained with small numbers of buyers and sellers with no knowledge of others’ costs or values. 3. Another reason for our interest in small decisions is the feeling that external validity of laboratory research is larger in the context of small decisions that are similar to the laboratory tasks in many ways (e.g., low stakes, limited decision time) than in the context of large decisions. So, we have more to say about small decisions. 4. Erev and Livene-Tarandach (2005) showed that standardized experimental paradigms could be used to reduce differences between natural sciences and social sciences. Many exam questions in the natural sciences (about 64% in the sample of physics GRE exams used to evaluate applicants to graduate school) and few questions in the social sciences (about 10% of the questions in psychology GRE exams) require predictions. The focus on standardized experimental paradigms could be used to reduce this gap by facilitating the development of short and clear prediction questions in the social sciences. 5. The payoff variability effect is related to the role of flat payoff functions. Harrison (1989) notes that the deviation from maximization (and equilibrium) observed in many experimental studies can be a product of the low expected cost of these deviations relative to the required effort to find the optimal choice. Merlo and Schotter (1992) refine this assertion and note that there may be large differences between the expected and the experienced costs. The payoff variability effect suggests that the best predictor of these deviations is the relative cost: the average cost relative the payoff variance. This suggestion is consistent with Harrison assertion under the assumption that payoff variability is one of the factors that increases the effort required to find the optimal choice. 6. The probability mixture (B, p) denotes a win prospect B with probability p and 0 otherwise. 7. Additional research suggests that the importance of rare events is best approximated by the difference in expected values relative to payoff variance. 8. In addition to this competition, Erev et al. (2010a) organized a competition that focused on decisions from description and a competition that focused on decisions based on free sampling. The comparison of the three competitions clarifies the robustness of the experience-description gap. 9. The advantage of I-SAW does not appear to be a result of the larger number of parameters. Some of the submitted reinforcement learning models have the same number of parameters as the best model. More

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10. 11. 12.

13.

14.

15. 16.

17.

importantly, the competition method focuses on a prediction task, and for that reason addresses the risk of overfitting the data. ACT-R (adaptive control of thought—rational) is general theory of cognition (see Anderson and Lebiere 1998). Herrnstein et al. (1993, 150) write: “Melioration can be represented analytically as a type of partial maximization in which certain indirect effects are ignored or underweighted.” Nash equilibrium is defined as a prediction of the strategies of the different players from which no player has an incentive to deviate. That is, if a player believes that his or her opponent will follow a particular Nash prediction, he or she cannot benefit by deviating from this prediction. An equilibrium is weak if a deviation does not change the deviator’s payoff. Dal Bó (2005) ran repeated PD games with and without a fixed termination period. He found that in games without a fixed termination period, akin to infinitely repeated games, the “shadow of the future” significantly reduces opportunistic behavior. It is important to stress that the summary of these results is based on using I-SAW as a benchmark and incorporating cognitive strategies to explain the observed deviations from the predictions of this benchmark. Different research methodologies may lead to other insights. Econometric investigation (e.g., Camerer and Ho 1999) can be useful, but insights tend to be sensitive to the assumption that the underlying model is well calibrated (see Feltovich 2000; Salmon 2001; Wilcox 2006; Erev and Haruvy 2005). Insights can also be derived from the long-term convergence properties of simple models (see Milgrom and Roberts 1990; Kalai and Lehrer 1993; Kandori, Mailath, and Rob 1993; Fudenberg and Levine 1998; Hart and Mas-Colell 2001), but insights are limited to situations with very long horizons and stationary payoffs. The seating map can be used as evidence of cheating in the case of a disciplinary action to demonstrate that the students who have similar exam answers were also sitting next to one another. By some accounts, the demise of Dr. Semmelweis was a function of his research (or correction) decisions. It seems that the influential heads of the departments who were responsible for the high and avoidable death rates were unhappy with his results. We use the term inventions to refer to both naturally evolving institutions and to the outcomes of explicit mechanism design. The most important inventions, including the wheel, are the product of a process that includes natural evolution (e.g., people that rolled logs were more likely to survive) and some explicit design (e.g., the use of rubber to produce more effective wheels).

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Chapter 10 Sarin, R. and F. Vahid. 1999. Payoff Assessments without Probabilities: A Simple Dynamic Model of Choice. Games and Economic Behavior 28: 294–309. ———. 2001. Predicting How People Play Games: A Simple Dynamic Model of Choice. Games and Economic Behavior 34(1): 104–22. Sutton, R. S., and A. G. Barto. 1998. Reinforcement Learning: An Introduction. Cambridge, MA: MIT Press. Schmalensee, R. 1975. Alternative Models of Bandit Selection. Journal of Economic Theory 10: 333–42. Schultz, W. 1998. Predictive Reward Signal of Dopamine Neurons. Journal of Neurophysiology 80(1): 1–27. Schurr, A., D. Rodensky, and I. Erev. 2014. The Effect of Unpleasant Experiences on Evaluation and Behavior. Journal of Economic Behavior & Organization 106: 1–9. Segal, M. W. 1974. Alphabet and Attraction: An Unobtrusive Measure of the Effect of Propinquity in a Field Setting. Journal of Personality and Social Psychology 30: 654–57. Selten, R., and R. Stoecker. 1986. End Behaviour in Sequences of Finite Prisoner’s Dilemma Supergames: A Learning Theory Approach. Journal of Economic Behavior & Organization 7: 47–70. Shachat, J. M. 2002. Mixed Strategy Play and the Minimax Hypothesis. Journal of Economic Theory 104(1): 189–226. Shafir, S. 2000. Risk-Sensitive Foraging: The Effect of Relative Variability. Oikos 88: 663–69. Shafir, S.,T. Reich, E. Tsur, I. Erev, and A. Lotem. 2008. Perceptual Accuracy and Conflicting Effects of Certainty on Risk-Taking Behaviour. Nature 453: 917–20. Shanks, D. R., R. J. Tunney, and J. D. McCarthy.2002. A Re-Examination of Probability Matching and Rational Choice. A Journal of Behavioral Decision Making 15(3): 232–50. Sherman, R. 1971. Empirical Oligopoly. Kyklo 24(1): 30–49. Shteingart, H., T. Neiman, and Y. Loewenstein. 2013. The Role of First Impression in Operant Learning. Journal of Experimental Psychology: General 142(2): 476. Sidowski, J. B., L. B. Wyckoff, and L. Tabory. 1956. The Influence of Reinforcement and Punishment in a Minimal Social Situation. Journal of Abnormal and Social Psychology 52: 115–19. Siegel, S., and D. A. Goldstein. 1959. Decision-Making Behavior in a Two-Choice Uncertain Outcome Situation. Journal of Experimental Psychology 57: 37–42. Silverman, E. B. 1999. New York Police Department Battles Crime. Boston: Northeastern University Press. Simon, H. 1957. Models of Man: Social and Rational. New York: Wiley. Simonsohn, U., N. Karlsson, G. Loewenstein, and D. Ariely. Forthcoming. The Tree of Experience in the Forest of Information: Overweighing Experienced Relative to Observed Information. Games and Economic Behavior. Skinner, B. F. 1938. The Behavior of Organisms. New York: Appleton-Century-Crofts. Skogan, W. G. 1990. Disorder and Decline: Crime and the Spiral of Decay in American Neighborhoods. Berkeley, CA: University of California Press. ———. 1953. Science and Human Behavior. New York: Free Press. Slonim R. 2007. Empirical Regularities in Behavior across a Population of Games. Working paper. Slonim, R., and A. E. Roth. 1998. Learning in High Stakes Ultimatum Games: An Experiment in the Slovak Republic. Econometrica 66(3): 569–96. Smalley, W., D. Shatin, D. K. Wysowski, J. Gurwitz, S. E. Andrade, M. Goodman, K. A. Chen, R. Platt, S. D. Schech, and W. A. Ray. 2000. Contraindicated Use of Cisapride: Impact of Food and Drug Administration Regulatory Action. Journal of the American Medical Association 284(23): 3036–39. Smith, T. G., and A. Tasnádi. 2007. A Theory of Natural Addiction. Games and Economic Behavior 59: 316–44. Smith, V. L. 1962. An Experimental Study of Competitive Market Behavior. Journal of Political Economics 70: 111–37.

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EDITORS AND CONTRIBUTORS EDITORS John H. Kagel is University Chaired Professor of Applied Economics and Director of the Economics Laboratory at The Ohio State University. He has published widely in leading economic, psychology and political science journals on topics ranging from group versus individual behavior in strategic interactions, auctions, legislative bargaining, and individual choice. He has held previous positions at University of Pittsburgh, University of Houston, and Texas A&M. He is a fellow of the Econometric Society. Alvin E. Roth is the McCaw Professor of Economics at Stanford and the Gund Professor of Economics and Business Administration Emeritus at Harvard. He earlier taught at the University of Pittsburgh and the University of Illinois. Together with Lloyd Shapley, he shared the 2012 Nobel memorial prize in Economics. Together with John Kagel he edited the 1995 Handbook of Experimental Economics.

OTHER CONTRIBUTORS Colin F. Camerer is the Robert Kirby Professor of Behavioral Economics at Caltech, California. He specializes in applying diverse methods from psychology and neuroscience to test theories of choices, games, and markets experimentally. He also uses field data to test theories from behavioral economics. He is past president of the Economic Science Association and Society for Neuroeconomics, and received a MacArthur Fellowship in 2013. Jonathan D. Cohen is the Robert Bendheim and Lynn Thoman Bendheim Professor of Neuroscience, Professor of Psychology, and Co-Director of the Princeton Neuroscience Institute at Princeton University. He studies the human capacity for cognitive control— the ability to pursue goal-directed behavior in the face of distraction or interference— and its disturbance in psychiatric disorders. His work draws on a combination of behavioral, human brain–imaging, computational modeling, and mathematical analysis methods to identify and characterize the neural mechanisms underlying cognitive control. He is a recipient of the American Psychological Association Distinguished Scientific Contribution Award and a Fellow of the American Psychological Society and the American Association for the Advancement of Science. David J. Cooper holds the Brim Eminent Scholar Chair in economics at Florida State University in Tallahassee, Florida, and serves as chair of the executive committee for xs/fs, the experimental social sciences cluster at FSU. Previously he has held appointments at the University of East Anglia, Case Western Reserve University, and the University of Pittsburgh. His work in experimental economics has focused on learning, play by teams, communication, and coordination. Cooper serves as editor-in-chief for Experimental Economics.

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John Duffy is professor of economics at the University of California, Irvine. His research concerns the microfoundations of macroeconomic behavior, with a particular focus on the manner in which individuals form forecasts, learn over time, and resolve coordination problems. He has used theoretical, experimental and computational methods to address these topics. Ido Erev (PhD in quantitative psychology from UNC in 1990) is a professor of behavioral sciences and economics at the Technion and a research environment professor at Warwick Business School. His research tries to clarify the conditions under which wise incentive systems can solve behavioral and social problems. In order to achieve this goal, Dr. Erev and his coauthors study choice behavior in the laboratory, develop and compare alternative models, and evaluate the implications of the results in intervention studies. Their research reveal a robust experience-description gap: People exhibit oversensitivity to rare events when they decide based on a description of the incentive structure, but experience reverses this bias and lead to underweighting of rare events. Comparison of alternative models favors the assumption that people tend to select the option that led to the best outcome in a small sample of similar past experiences. These observations imply that incentives are most effective when they insure that the socially desirable behavior maximizes payoff, and minimizes the probability of regret. Ernst Fehr has been professor of microeconomics and experimental economics at the University of Zurich since 1994 and a global distinguished professor at New York University since 2011. He also serves as director of the UBS International Center of Economics in Society. Dr. Fehr’s research focuses on the interplay between social preferences, social norms, and strategic interactions and on how society and biology affect human preferences. His work is characterized by the combination of game theoretic tools with experimental methods and the use of insights from economics, social psychology, sociology, biology, and neuroscience for a better understanding of human social behavior. More detailed information about Dr. Fehr’s research can be found at http://www.econ.uzh.ch/en/people/faculty/fehr.html; most of his papers are available for download from this site. Guillaume R. Fréchette is a professor of economics and political science at New York University. His work mostly uses experimental methods, and many of his papers fall under the heading of bargaining or repeated games. The work on bargaining started by studying models of legislative bargaining but recently has moved to investigating reputation. Repeated interactions, in particular in social dilemmas, offered another important area of investigation. That work focuses on the determinants of cooperation and the strategies people adopt to support cooperation. His website can be found at www.cess.nyu.edu/frechette where all of his papers can be downloaded. Paul W. Glimcher is Julius Silver Professor of Neural Science, Economics and Psychology at New York University. He is also director of the Institute for the Interdisciplinary Study of Decision Making. His work is focused on the intersection of economics and neurobiology. He develops novel economic models that include constraints derived from normative and positive studies of neural representation. His research has appeared in academic journals ranging from Science and Nature to The Quarterly Journal of Economics to Nature Neuroscience. He is the lead editor of the standard textbook in neuroeconomics: Neuroeconomics: Decision Making and the Brain. His recently published book Foundations of Neuroeconomic Analysis is widely considered foundational for this new field.

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Ernan Haruvy is a professor of marketing at the University of Texas at Dallas. He specialties in behavioral and experimental economics. He has worked on applying behavioral models using experimental methods, data analysis, and economic theory to improve the design of markets, including applications in auctions, procurement, electronic commerce, sponsored search, and software markets. David Laibson is the Robert I. Goldman Professor of Economics and chairman of the Department of Economics at Harvard University. He leads Harvard University’s Foundations of Human Behavior Initiative. Dr, Laibson’s research focuses on the topic of behavioral economics, with emphasis on household finance, macroeconomics, aging, and intertemporal choice. Dr. Laibson is also a member of the National Bureau of Economic Research, where he codirects the National Institute of Aging Roybal Center for Behavior Change in Health and Savings and is a Research Associate in the Aging, Asset Pricing, and Economic Fluctuations Working Groups. Dr. Laibson serves on the board of the Russell Sage Foundation and on Harvard’s Pension Investment Committee. He also serves on the advisory board of the Social Science Genetics Association Consortium and has served on the Academic Research Council of the Consumer Financial Protection Bureau. Dr. Laibson is a recipient of a Marshall Scholarship. He is a fellow of the Econometric Society and the American Academy of Arts and Sciences and is a recipient of the TIAA-CREF Paul A. Samuelson Award for Outstanding Scholarly Writing on Lifelong Financial Security. Dr. Laibson holds degrees from Harvard University (AB in Economics, Summa), the London School of Economics (MSc in Econometrics and Mathematical Economics), and the Massachusetts Institute of Technology (PhD in Economics). He received his PhD in 1994 and has taught at Harvard since then. In recognition of his teaching, he has been awarded Harvard’s BK Prize and a Harvard College Professorship. Dan Levin is a professor of economics at The Ohio State University, a College of Social and Behavioral Sciences Distinguished Professor, and a Distinguished University Scholar. His major research interests are in the area of auctions and competitive bidding. His research, often funded by the NSF, involves both theoretical and experimental methodologies. He studies price formation, information processing by bidders and its aggregation, the role of competition, and learning. Another general area of interest is industrial organization, focusing on the relationship between market structures and market performance and modeling entry in static and dynamic environments. More recently Dr. Levin has extended his interests to behavioral economics under risk and ambiguity. Dr. Levin has published more than fifty-five peer-refereed papers, with many in the top five journals, and more than twenty-five papers in the top ten. He is a fellow of the Society for the Advancement of Economic Theory and a fellow of the Department of Economics at The Hebrew University in Jerusalem. He has served on the National Science Foundation Economics Advisory Panel and twice on the NSF Knowledge and Distributed Intelligence panel. He was a Visiting Scholar at Harvard from August 2002 to June 2003, a Visiting Professor at Stanford University from December 2006 to March 2007 and again from January to June 2016, and a Visiting Professor at the University of California in Berkeley, from January to May 2014. He has done many shorter visits to various universities, including Johns Hopkins, Yale, Tel Aviv, Hebrew, and Paris School of Economics. Muriel Niederle is a professor of Economics at Stanford University and a member of the National Bureau of Economic Research. One of her main fields is

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behavioral/experimental economics; she has also worked on market design. She is known for her work on gender differences, especially on gender differences in competitiveness. She has a blog at http://experimentalandbehavioral.blogspot.com/ that she operates intermittently. Thomas R. Palfrey is the Flintridge Foundation Professor of Economics and Political Science at the California Institute of Technology. He specializes in the application of game-theoretic models to political science and economics and laboratory experimental methods in economics, political science, and game theory. His research is published in the leading academic journals of economics, political science, and game theory. He is former editor of Games and Economic Behavior and has served on many editorial boards, including Econometrica, Journal of Public Economics, Economic Theory, and AEJ Micro. He was the founding director of the Hacker Social Science Experimental Laboratory at Caltech and the Princeton Laboratory for Experimental Social Science. He is a fellow of the Econometric Society, the American Academy of Arts and Sciences, and the Society for the Advancement of Economic Theory. He is former president of the Economic Science Association and council member of the Game Theory Society. He has just completed a book on quantal response equilibrium, coauthored with Jacob Goeree and Charles Holt, which is forthcoming from Princeton University Press. Lise Vesterlund is the Andrew W. Mellon Professor and Chair of the Department of Economics at the University of Pittsburgh. Her research focuses on understanding how and why we give to charity and on why men are more successful than women in climbing the corporate ladder. Her research is posted at http://www.pitt.edu/~vester/.

ILLUSTRATION CREDITS

CHAPTER 1 1.1 Parts of Figures 4 and 7 on pages 557 and 564 of Vivian Lei and Charles N. Noussair. “An Experimental Test of an Optimal Growth Model.” American Economic Review 92, no. 3 (2002): 549–570. 1.2 Part of Figure 1 on page 1316 of Rosemarie Nagel. “Unraveling in Guessing Games: An Experimental Study.” American Economic Review 85, no. 5 (1995): 1313–1326. 1.3 Cars Hommes, Joep Sonnemans, Jan Tuinstra, and Henk van de Velden. “Learning in Cobweb Experiments.” Macroeconomic Dynamics (2007). 1.4 ©Monica C. Capra, Tomomi Tanaka, Colin F. Camerer, Lauren Feiler, Veronica Sovero, and Charles N. Noussair. Economic Journal (2009). ©Royal Economic Society. 1.6 Cary A. Deck, Kevin A. McCabe, and David P. Porter. “Why Stable Fiat Money Hyperinflates: Results from an Experimental Economy.” Journal of Economic Behavior & Organization, no. 3 (2006). 1.8 Figure 1 on page 1251 of Ernst Fehr and Jean-Robert Tyran. “Does Money Illusion Matter?” American Economic Review 91, no. 5 (2001): 1239–1262. 1.9 Ernst Fehr, Georg Kirchsteiger, and Arno Riedl. “Does Fairness Prevent Market Clearing? An Experimental Investigation.” Quarterly Journal of Economics, no. 2 (1993). 1.10 Charles N. Noussair et al. “The Principles of Exchange Rate Determination in an International Finance Experiment.” Journal of Political Economy (1997). 1.11 Peng Lian and Charles R. Plott. “General Equilibrium, Markets, Macroeconomics and Money in a Laboratory Experimental Environment.” Economic Theory, no. 1 (1998). 1.12 ©2007, John Wiley and Sons. 1.13 John Van Huyck et al. “Is Reputation a Substitute for Commitment in the Peasant-Dictator Game?” (2001). 1.14 ©The Association of the International Journal of Central Banking (IJCB). 1.15 Tiziana Assenza, Peter Heemeijer, Cars Hommes, Domenico Massaro. “Individual Expectations and Aggregate Macro Behavior.” (2012).

CHAPTER 2 2.2 Reprinted from Jacob K. Goeree, Charles A. Holt, and Susan K. Laury. “Private Costs and Public Benefits: Unraveling the Effects of Altruism and Noisy Behavior.” Journal of Public Economics 83, no. 2 (2002): 255–276. ©2002, with permission from Elsevier. 2.3 Dan Ariely, Anat Bracha, and Stephan Meier. “Doing Good or Doing Well? Image Motivation and Monetary Incentives in Behaving Prosocially.” American Economic Review (2009): 544–555. 2.4 James Andreoni and B. Douglas Bernheim. “Social Image and the 50–50 Norm: A Theoretical and Experimental Analysis of Audience Effects.” Econometrica (2009): 16. 2.5 Jan Potters, Martin Sefton, and Lise Vesterlund. “Leading-by-Example and Signaling in Voluntary Contribution Games: An Experimental Study.” Economic Theory (2007): 169–182. 2.6 John Morgan and Martin Sefton. “Funding Public Goods with Lotteries: Experimental Evidence.” Review of Economic Studies, no. 4 (2000).

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CHAPTER 3 3.6 Giorgio Coricelli and Rosemarie Nagel. “Neural Correlates of Depth of Strategic Reasoning in Medial Prefrontal Cortex.” PNAS, no. 23 (2009).

CHAPTER 4 4.1 Robert Forsythe, Joel L. Horowitz, N. E. Savin, and Martin Sefton. “Fairness in Simple Bargaining Experiments.” Games and Economic Behavior, no. 3 (1994). 4.2 Sally Blount. “When Social Outcomes Aren’t Fair: The Effect of Casual Attributions on Preferences.” Organizational Behavior and Human Decision Processes, no. 2 (1995). 4.3 ©2007, John Wiley and Sons. 4.4 John H. Kagel and Katherine Wolfe. “Tests of Fairness Models Based on Equity Considerations in a Three-Person Ultimatum Game.” Experimental Economics, no. 3 (2001): 210. 4.5 Yoella Bereby-Meyer and Muriel Niederle. “Fairness in Bargaining.” Journal of Economic Behavior & Organization, no. 2 (2005). 4.6 David J. Cooper and E. Glenn Dutcher. “The Dynamics of Responder Behavior in Ultimatum Games: A Meta-study.” Experimental Economics, no. 4 (2011): 529. 4.7 David J. Cooper and Carol Kraker Stockman. “Fairness and Learning: An Experimental Examination.” Games and Economic Behavior, no. 1 (2013). 4.8 James C. Cox. “How to Identify Trust and Reciprocity.” Games and Economic Behavior, no. 2 (2004). 4.9 Jason Dana, Roberto A. Weber, and Jason Xi Kuang. “Exploiting Moral Wiggle Room: Experiments Demonstrating an Illusory Preference for Fairness.” Economic Theory, no. 1 (2007): 72. 4.10 ©2005, John Wiley and Sons. 4.11 Jason Dana, Roberto A. Weber, and Jason Xi Kuang. “Exploiting Moral Wiggle Room: Experiments Demonstrating an Illusory Preference for Fairness.” Economic Theory, no. 1 (2007): 73. 4.12 Bjorn Bartling and Urs Fischbacher. “Shifting the Blame: On Delegation and Responsibility.” Review of Economic Studies, no. 1 (2012): 67–87. 4.13 Ernst Fehr, Georg Kirchsteiger, and Arno Riedl. “Does Fairness Prevent Market Clearing? An Experimental Investigation.” Quarterly Journal of Economics, no. 2 (1993): 447. 4.14 Lynn Hannan. “The Combined Effect of Wages and Firm Profit on Employee Effort.” Accounting Review (2005): 180. 4.15 Lynn R. Hannan et al. “Partial Gift Exchange in an Experimental Labor Market: Impact of Subject Population Differences, Productivity Differences, and Effort Requests on Behavior.” Journal of Labor Economics (2002). 4.16 Uri Gneezy and J. List. “Putting Behavioral Economics to Work: Field Evidence of Gift Exchange.” Econometrica (2006). 4.17 Sebastian Kube, Michel André Maréchal, and Clemens Puppe. “Do Wage Cuts Damage Work Morale? Evidence from a Natural Field Experiment.” Journal of the European Economic Association (2013). 4.18 Sebastian Kube, Michel André Maréchal, and Clemens Puppe. “The Currency of Reciprocity: Gift Exchange in the Workplace.” American Economic Review (2012): 1650.

CHAPTER 5 5.1 Jacob K. Goeree and Charles Holt. “Hierarchical Package Bidding: A Paper & Pencil Combinatorial Auction.” Games and Economic Behavior, no. 1 (2010). 5.4 Gary Bolton, Ben Greiner, and Axel Ockenfels. “Engineering Trust: Reciprocity in the Production of Reputation Information.” Management Science 59, no. 2 (2013): 265–285.

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CHAPTER 6 6.1–6.3 Morris P. Fiorina and Charles R. Plott. “Committee Decisions under Majority Rule: An Experimental Study.” American Political Science Review (1978). 6.4 Charles R. Plott and Michael E. Levine. “A Model of Agenda Influence on Committee Decisions.” American Economic Review, no. 1 (1978): 146–160. 6.5 Guillaume R. Frechette, John H. Kagel, and Massimo Morelli. “Pork versus Public Goods: An Experimental Study of Public Good Provision within a Legislative Bargaining Framework.” Economic Theory (2012). 6.6 Marco Battaglini and Thomas R. Palfrey. “The Dynamics of Distributive Politics.” Economic Theory, no. 3 (2012). 6.7–6.8 Marco Battaglini, Salvatore Nunnari, and Thomas R. Palfrey. “Legislative Bargaining and the Dynamics of Public Investment.” American Political Science Review (2012). 6.9–6.10 Richard D. McKelvey and Peter C. Ordeshook. “Elections with Limited Information: A Fulfilled Expectations Model Using Contemporaneous Poll and Endorsement Data as Information Sources.” Journal of Economic Theory (1985). 6.11 Kenneth E. Collier et al. “Retrospective Voting: An Experimental Study.” Public Choice, no. 2 (1987). 6.12 Charles R. Plott. “A Comparative Analysis of Direct Democracy, Two-Candidate Elections, and Three-Candidate Elections in an Experimental Environment.” In: Laboratory Research in Political Economy, Thomas Palfrey (ed.), University of Michigan Press, Ann Arbor, 1991. 6.13–6.14 David K. Levine and Thomas R. Palfrey. “The Paradox of Voter Participation? A Laboratory Study.” American Political Science Review, no. 1 (2007).

CHAPTER 8 8.5 Gary E. Bolton and Elena Katok. “An Experimental Test for Gender Differences in Beneficent Behavior.” Economics Letters, nos. 3–4 (1995): 287–292. 8.6 James Andreoni and Lise Vesterlund. “Which Is the Fair Sex? Gender Differences in Altruism.” Quarterly Journal of Economics, no. 1 (2001). 8.7 Lise Vesterlund, Linda Babcock, and Laurie Weingart. “Breaking the Glass Ceiling with ‘No’: Gender Differences in Declining Requests for Non-promotable Tasks.” Working paper (2014). 8.9 Charles A. Holt and Susan K. Laury. “Risk Aversion and Incentive Effects.” American Economic Review, no. 5 (2002): 1644–1655. 8.10 Paul Slovic. “Information Processing, Situation Specificity, and the Generality of Risk-Taking Behavior.” Journal of Personality and Social Psychology, no. 1 (1972): 128–134.

CHAPTER 9 9.1 R. M. Isaac and Duncan James. “Just Who Are You Calling Risk Averse?” Journal of Risk and Uncertainty, no. 2 (2000): 183. 9.2 Robert Dorsey and Laura Razzolini. “Explaining Overbidding in First Price Auctions Using Controlled Lotteries.” Experimental Economics, no. 2 (2003): 132. 9.3 Rodney Garratt, Mark Walker, and John Wooders. “Behavior in Second-Price Auctions by Highly Experienced eBay Buyers and Sellers.” Experimental Economics, no. 1 (2012): 51. 9.4 Gary Charness and Dan Levin. “The Origin of the Winner’s Curse: A Laboratory Study.” American Economic Journal: Microeconomics 1, no. 1 (2009): 207–236. 9.5 Gary Charness and Dan Levin. “The Origin of the Winner’s Curse: A Laboratory Study.” American Economic Journal: Microeconomics 1, no. 1 (2009): 221. 9.6 Jacob K. Goeree and Theo Offerman. “Efficiency in Auctions with Private and Common Values: An Experimental Study.” American Economic Review (2002): 631. 9.7 John H. Kagel and Dan Levin. “Behavior in Multi-unit Demand Auctions: Experiments with Uniform Price and Dynamic Vickrey Auctions.” Econometrica (2001): 429.

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Credits 9.8 John H. Kagel and Dan Levin. “Behavior in Multi-unit Demand Auctions: Experiments with Uniform Price and Dynamic Vickrey Auctions.” Econometrica (2001): 431. 9.9 John H. Kagel and Dan Levin. “Behavior in Multi-unit Demand Auctions: Experiments with Uniform Price and Dynamic Vickrey Auctions.” Econometrica (2001): 442. 9.10–9.11 ©2006 John Wiley and Sons. 9.12 Owen R. Phillips, Dale J. Menkhaus, and Kalyn T. Coatney. “Collusive Practices in Repeated English Auctions: Experimental Evidence on Bidding Rings.” American Economic Review (2003): 972. 9.13 Theo Offerman and Jan Potters. “Does Auctioning the Entry Licences Induce Collusion? An Experimental Study.” Review of Economic Studies, no. 3 (2006).

NAME INDEX Abbink, Klaus, 237, 465 Abraham, D., 335n9 Adam, K., 17–18, 71 Akerlof, G. A., 7, 47, 81n36, 253, 260, 266, 270 Albrecht, Konstanze, 179–80 Alevy, J. E., 464 Ali, Nageeb, 403–4 Aliprantis, C. D., 2 Allais, M., 441, 443, 458, 469, 647, 648 Allyon, T., 449 Almås, Ingvild, 494 Alos-Ferrer, Carlos, 677 Al-Ubaydli, O., 269–70 Amodio, D. M., 198 Anbarci, N., 34, 42 Andersen, Steffen, 178, 458, 459, 470 Anderson, Lisa R., 677 Anderson, S., 14, 98, 256–57 Andreoni, James, 95–97, 100–102, 106–7, 109–12, 133n8, 135nn26, 31, 137n58, 138n67, 139n74, 225, 229, 235, 246–47, 275, 277n12, 278nn33, 37, 513, 516–20, 571–72, 625n20, 686 Ansic, David, 534 Ansolabehere, Stephen, 372 Apesteguia, Jose, 685 Apicella, Coren L., 492 Aragones, Enriqueta, 391 Arbak, Emrah, 117–18 Ariely, Dan, 105–6, 115, 140n96, 309–13, 485–86, 618 Arifovic, James, 26–27, 65–67, 279n41, 684 Arkes, Michael, 282n98 Armantier, Olivier, 278n37, 566 Ashenfelter, O., 576 Ashraf, Nava, 179 Assenza, T., 70–71 Atkinson, Richard C., 680–81 Austen-Smith, David, 400–401 Ausubel, L. M., 599, 602, 604, 627n65, 628n66 Avery, C., 588–89 Ayres, Ian, 317 Azariadis, C., 27 Azrieli, Yaron, 526–27, 550n40 Azrin, N. H., 449 Babcock, Linda, 523, 525 Bagnoli, Mark, 111, 136n47 Bajari, P., 569 Balafoutas, Loukas, 496, 548n14 Baldiga, Katherine A., 544–45, 553n71 Ball, Michael O., 299

Ball, Sheryl, 117 Balliet, Daniel, 521, 550n36 Ballinger, T. P., 8–9 Bandura, A., 677 Banks, J., 299, 400–401 Bao, T., 18–19 Baran, Nichole M., 257–58 Bardsley, Nicholas, 106, 108, 245, 513 Baron, David P., 242, 366–69 Barro, R. J., 61, 64 Barron, G., 644, 647–50, 673, 693–94 Bartling, Björn, 135n32, 249, 252 Basmann, Robert, 449–50 Bassi, Anna, 388 Bateson, Melissa, 135n33 Battaglini, Marco, 374–76, 378–81, 405, 407–9 Battalio, Raymond C., 47, 64–65, 438–42, 449–51, 469 Baumgartner, Thomas, 188 Bazerman, M. H., 294 Bechara, A., 656–57 Becker, Anke, 264 Becker, Gary S., 201n5, 445, 449, 565 Beil, Damian R., 579 Bekkers, Rene, 473n27 Bellamere, Charles, 270, 281n91, 455–57, 470, 471 Belot, Michele, 459–60, 470 Bénabou, Roland, 105, 135n30 Benartzi, Shlomo, 132 Benhabib, Jess, 14, 178 Ben-Ner, Avner, 518 Ben Zion, U., 645 Bereby-Meyer, Yoella, 228–29, 646–47, 686 Berentsen, A., 34 Berg, Joyce E., 240, 260, 513 Bergstrom, Theodore, 93 Berl, Janet, 357 Berman, E., 697 Bernasconi, M., 34, 37–38, 73–74 Bernhard, Helen, 255 Bernheim, B. Douglas, 106–7, 110, 225, 246–47, 513 Berry, Timothy R., 448 Bertrand, Marianne, 484 Besedeš, Tibor, 454 Beshears, John, 179 Bettinger, Eric, 448, 470, 473n16 Betz, Nancy E., 540 Bhatt, Meghana, 191, 198, 199 Bikchandani, S., 588 Binmore, Kenneth, 236–38, 301

726

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Name Index Bishara, A. J., 650 Bisin, Alberto, 178 Blais, Ann-Renée, 540, 651 Blanchard, Emily, 278n37 Blanco, Mariana, 244 Blinder, A. S., 67–69 Blount, Sally, 220–21, 275–76 Blum, A., 335n9 Blume, A., 24 Blume, Lawrence, 93 Bohnet, Iris, 549n30 Bolton, Gary E., 100, 102, 135n26, 217, 219, 222–26, 229–32, 247–49, 265, 277n11, 280n63, 314–16, 446, 515 Bordalo, Pedro, 553n72 Bosch-Domènech, Antoni, 59–60, 457, 471 Bossaerts, P., 194–95, 198 Boynton, Geoffrey M., 167 Bracha, Anat, 105–6, 112, 115, 133n7, 135n34, 140n96, 508 Brams, S., 414–15 Brandts, Jordi, 231 Braunstein, Y. M., 46 Braver, Todd S., 167, 168 Breman, Anna, 132 Brinig, M. F., 534 Brodmann, Corbinian, 163 Bronars, Stephen G., 96 Brosig, J., 231, 608–9, 628n72 Brown, A. L., 11–12, 628n78 Brown, Eleanor, 520 Brown, J. N., 682 Brown, M., 46, 262 Brown, Paul M., 34, 39–40, 109–10, 137n58, 277n12 Brusco, S., 611 Buchanan, James, 414 Budescu, D. V., 683 Budish, Eric, 331–33 Bühren, Christoph, 466–67, 471 Bulfin, Robert L., 297–98 Bull, Clive, 391 Buraˇcas, Giedrius, 167 Burghart, Daniel R., 103, 184–85 Burks, Stephen V., 264 Burns, P., 462–63, 571, 625n31 Burock, Marc A., 167 Busemeyer, J. R., 643, 645, 650, 657, 673 Buser, Thomas, 504, 507, 510, 536, 543 Bush, George W., 639 Byrnes, James P., 528, 533, 535, 551n51 Cabrales, A., 32, 77 Cadsby, C. Bram, 61–63, 464, 491, 495 Cain, Daylian M., 245–46, 276 Calsamiglia, Caterina, 549n22 Calvo, G., 71 Camera, G., 34, 38, 42

Camerer, Colin F., 11, 15, 138n73, 153, 154, 181, 185, 191, 193, 198, 199 Cameron, Lisa A., 219 Campbell, W. M., 293, 597 Cantillon, Estelle, 331–32 Capen, E. C., 293, 597 Capra, C. M., 22–23, 80n21 Carbone, E., 5–6, 11–12 Cárdenas, Juan-Camilo, 495, 501, 502 Carlson, John, 2 Carlsson, H., 30, 80n27 Carpenter, Jeffrey, 125, 140n96, 256, 457, 460, 464, 470 Carter, John R., 399 Casari, Marco, 34, 42, 231, 594–95 Casella, Alessandra, 411–12, 415–17 Cason, Timothy N., 231, 490, 567 Cass, D., 4, 27 Cassady, Ralph, 299 Chamberlin, Edward H., 290–91 Chambers, Christopher P., 526–27, 550n40 Chammah, Albert M., 520, 684–85 Chan, Kenneth S., 134n25 Charness, Gary, 138n69, 218, 230, 231, 233–35, 243, 244, 254, 275–76, 278n28, 436, 453, 470, 494, 535, 552n58, 590–92, 625n51 Che, Y. K., 571–72, 625n20 Chen, M. Keith, 173, 442–43, 469 Chen, Y., 254–55, 605 Chernomaz, K., 574–75, 606 Cherry, Todd L., 237, 280n58 Cheung, Yin-Wong, 370, 660 Chiu, P. H., 196 Choi, Syngioo, 119 Chong, K., 191 Chua, Z. E., 11 Clapp, R. V., 293, 597 Clapton, Eric, 125 Clarke, E., 604–5 Cleave, Blair L., 256 Coatney, K. T., 611 Coffman, Katherine B., 512, 516 Coffman, Lucas C., 135n32, 252–53 Cohen, Jacob, 513–14, 528–29, 536, 552n62 Cohen, Jonathan D., 153 Cohen, Linda, 362–63, 365 Cohn, A., 270, 274 Colander, D., 154 Coleman, R. Edward, 164 Coles, Peter, 328 Coller, Maribeth, 14, 458 Collier, Kenneth E., 384–86 Colman, A. A., 677–80 Condorcet, Marquis de, 352, 400 Conlin, Michael, 519–20 Connolly, Cristina, 457, 460 Connolly, Michelle, 336n15

Name Index Cooper, David J., 97, 137n53, 217, 237–38, 280n76, 463–65, 511–12, 549nn23, 24, 572 Cooper, Russell, 24, 136n43, 138n73 Corazzini, Luca, 125, 140n91 Corbae, D., 27 Coricelli, G., 190–93, 198 Cornand, C., 31–32 Cotton, Christopher, 500–501 Cox, James C., 241–42, 278n29, 281n91 Craig, A., 199, 520 Cramton, Peter, 316–17, 417, 590, 598 Crawford, G., 302, 305–6, 697 Crawford, V. P., 590, 626n46 Critchley, H. D., 199 Crockett, S., 8 Crosetto, Paolo, 535–37, 541, 545, 552n61 Croson, Rachel T. A., 115, 132, 254, 513, 518, 521, 533, 552n55, 665 Crowley, Maureen, 513, 549n25 Dal Bó, P., 12, 686, 702n13 Dale, Donald J., 121–22 Dana, Jason, 104–5, 245–47, 275, 276 Dardanoni, V., 4–5 Dasgupta, Sugato, 384 Da Silva, D. G., 628n72 Dato, Simon, 501 Davis, D., 18, 72–73, 128–30 Dawes, Robyn M., 245–46, 276 Deb, Rahul, 135n27 Deck, C. A., 34, 35 DeGroot, Morris H., 449, 565 DeJong, Douglas V., 462, 464 Delfgaauw, Josse, 504 DellaVigna, Stefano, 107–8, 179 De Martino, B., 173, 201n7 Denrell, J., 663, 696–97 De Oliveira, Angela, 140n103 de Quervain, Dominique J. F., 184, 186 de Sousa, Jose, 466–67 Deters, T., 113–14 Diamond, P., 27, 39, 43 Dickhaut, John, 240, 260, 513 Dickinson, D. L., 47 Dickson, Eric, 405 Diederich, A., 645 Diermeier, Daniel, 372 Di Guida, S., 662 Di Laurea, D., 63 Dohmen, Thomas, 264, 492, 534, 541–43 Dolan, R. J., 192, 193, 198 Dollard, J., 676 Donchin, E., 695 Donders, F. C., 166 Dorsey, Robert E., 118, 131–32, 138n68, 565–66 Dreber, Anna, 521 Druckman, J. N., 372 Duch, Raymond M., 459–60, 470

•

727

Duffy, J., 1, 2, 8, 11–12, 27–30, 32, 34, 39–43, 81n32, 118–19, 397 Dufwenberg, Martin, 234–35, 277n9, 517–18 Duncan, Brian, 140n103 Dunne, T., 628n72 Dutcher, E. Glenn, 238–39 Dweck, Carol, 510 Dwyer, Gerald P., Jr., 440–41 Dybvig, P., 27 Dyer, D., 464–65, 468, 596 Eagly, Alice H., 513, 549n25 Eavey, Cheryl, 357–58, 360–61, 368 Eckel, Catherine C., 117, 128–30, 140n103, 254, 280n66, 365–66, 482, 515–18, 520, 532–37, 545, 551nn53, 54 Edgeworth, Francis, 154 Edlund, Lena, 548n4 Eichenberger, Reiner, 244–45, 276 Einav, Liran, 337n26, 541 Einhorn, H. J., 663 Elbittar, A. A., 624n4 Elfenbein, Daniel W., 139n87 Eliaz, K., 615–16 Ely, Jeffrey C., 176, 338n33, 618 Engel, Christoph, 519 Engel, R., 624n3 Engelbrecht-Wiggans, R., 568–69, 578, 603–4, 619 Engelmann, Dirk, 231, 232, 244, 414, 603, 627n62 Engers, Maxim, 123, 124 Englemann, Dirk, 469–70 Engle-Warnick, J., 68–70 Erdem, T., 697 Erev, Ido, 137n50, 175, 236–38, 638, 643–51, 655, 657–58, 660, 662–69, 672–75, 677–78, 680–81, 687–88, 690–94, 696, 698–99, 701n4 Eriksson, Tor, 548n13 Ert, E., 646–47, 650–51, 662, 665, 675 Estes, W. K., 651 Exley, Christine L., 513 Falk, Armin, 49, 132, 225, 234, 255–56, 260–62, 282n96, 455–56, 473n25, 542–43 Fang, H., 572 Faravelli, Marco, 125, 140n91 Farquharson, Robin, 364 Feddersen, T., 399, 401, 402, 407 Fehr, Ernst, 30, 43–45, 48–50, 138n71, 153, 185, 217, 222–25, 229, 231, 232, 244, 255, 259–62, 265, 270, 274–76, 279n42, 282n96, 446, 457, 461, 464 Fehr-Duda, Helga, 534 Feinberg, R. M., 13 Feliz-Ozbay, Emel, 264 Felsenthal, Dan, 389 Ferejohn, John A., 242, 366–69 Fershtman, Chaim, 508 Fessler, Daniel M. T., 135n33

728

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Name Index Fey, M., 365 Figner, Bernd, 155, 181 Filippin, Antonio, 535–37, 541, 545, 552n61 Filiz, E., 568–69, 624n10 Finucane, Melissa L., 534 Fiorina, Morris, 352–58, 392 Fischbacher, Urs, 135n32, 138n71, 225, 234, 249, 252, 255, 282n96 Fischer, A. J., 399 Fisher, E. O’N., 28–30, 53–55 Fisher, F. M., 79n2 Fisher, Irving, 154 Fisman, Raymond, 96, 235–36, 520 FitzGerald, Thomas H. B., 175 Flinn, C. J., 46 Flory, Jeffrey A., 504 Forsythe, Robert, 219–20, 387–88, 390, 462, 464 Fouraker, Lawrence E., 461–62, 464, 470 Frank, Björn, 466–67, 471 Frank, M., 61–63 Franke, Jörg, 549n22 Fréchette, Guillaume R., 242–43, 369–74, 435–36, 462–64, 468, 686 Freeman, Richard B., 501 Freud, Sigmund, 181 Frey, Bruno S., 115–16 Friedman, Daniel, 138n69, 278n29, 370, 660 Friedman, Milton, 230, 696 Friston, K. J., 167, 192, 198 Frith, C. D., 198 Frykblom, Peter, 280n58 Fudenberg, Drew, 521 Fujikawa, T., 663 Funk, Patricia, 548n4 Gächter, Simon, 49, 110, 116, 137n58, 138nn65, 66, 71, 261–62, 265, 474n33, 521–23 Gado, Mokhtar, 164 Gailmard, Sean, 372 Gaissmaier, W., 670 Gale, Douglas, 119 Gale, John, 236–38 Gallagher, H. L., 190 Gans, N., 665 Garbarino, Ellen, 258 Garratt, R., 24–25, 570–71 Garvin, Susan, 137n53 Gathman, Christina, 548n4 Gavetti, G., 674 Gazzale, Robert S., 135n27 Gazzola, V., 199 Gelber, Alexander M., 501 Gelman, Andrew, 411–12 Genesove, D., 576 Georganas, S., 572 Gerardi, Dino, 404 Gerber, Alan, 389–90 Gibbons, M., 417

Gilat, S., 687–88 Gilligan, Carol, 513 Giuliani, Rudolph, 695 Gjerstad, Steve, 278n29 Glaeser, Edward, 242 Glätzle-Rützler, Daniela, 493, 496–97 Glazer, Amihai, 135n30, 135n34 Glimcher, Paul W., 153, 181, 194 Gneezy, Uri, 139n86, 267–68, 391, 467–68, 493, 495, 497–500, 502–3, 507, 513, 518, 521, 533, 535, 541, 545, 552nn55, 58 Goeree, Jacob K., 98–99, 123, 124, 135n29, 299–300, 302–5, 395–97, 404–5, 567, 575, 593, 621–23 Goette, Lorenz, 255, 274. See also Götte, L. Gonzalez, C., 650, 667, 672 Goodstein, E., 358 Gopher, D., 673, 695 Gordon, D. B., 64 Gordon, D. G., 683 Goswami, G., 610 Götte, L., 270. See also Goette, Lorenz Gourville, J. T., 697 Grant, D. A., 646 Green, Leonard, 47, 439–42, 470, 671 Greiner, Ben, 314–16, 698–99 Grether, David M., 291, 295–98, 334–35nn5–7, 538–39 Griffith, W. I., 254 Grill-Spector, Kalanit, 167 Grimm, Veronika, 277n19, 414, 603, 627n62 Groseclose, Tim, 391 Grosse, Niels D., 491, 497 Grosser, Jens, 397–98, 422n84 Grosskopf, B., 645–46, 675 Grossman, Philip J., 128–30, 140n103, 254, 280n66, 482, 515–18, 520, 532–37, 541, 545, 551nn53, 54 Groves, T., 604–5 Guarnaschelli, Serena, 401, 402, 404, 405 Guerette, S. D., 399 Günther, Christina, 501 Gupta, Nabanita Datta, 497 Güth, Werner, 116, 137n59, 225, 457, 461, 513, 574, 687–88 Guyer, M. J., 683 Gysler, M., 534 Hafer, Cathy, 405 Haigh, Michael S., 464 Hake, H. W., 646 Haley, Kevin J., 135n33 Ham, J. C., 580–81, 594–95 Hampton, A., 194–95, 198 Handy, Femida, 136n44 Hannan, R. Lynn, 49–50, 263, 265 Harbaugh, William T., 103, 135nn30, 37, 184–85, 444–49, 469–71, 473n17, 490, 492, 534, 539

Name Index Hare, Todd A., 181, 187, 198 Harnett, D. L., 462, 470 Harris, Christopher, 338n54 Harrison, Glenn W., 278n36, 534, 552n63, 596–97 Harstad, Ronald M., 303 Haruvy, Ernan, 175, 578–79, 638, 643–44, 696 Hasson, Uri, 168 Hayashi, T., 625n12 Hayden, B., 193 Healy, Andrew, 548n12 Healy, Paul J., 266–67, 526–27, 550n40 Heinemaan, F., 30–32 Hennig-Schmidt, Heike, 270–71 Hens, T., 34, 35–36 Herrera, Helios, 396 Herrmann, Benedikt, 474n33, 523, 549n30 Herrnstein, R. J., 671–72, 702n11 Hertwig, R., 649–50 Herzberg, Roberta, 357, 365, 420n24 Hey, J. D., 4–6 Hirshleifer, J., 278n36 Ho, T.-H., 191, 193 Hochman, G., 669 Hoffman, Elizabeth, 105 Hogarth, R. M., 663 Holländer, Heinz, 135n30 Hollard, Guillaume, 466–67, 469–70 Holm, Håkan, 454, 456, 471 Holmes, Jessica, 125 Holt, Charles A., 14, 98, 133n7, 135n29, 302–5, 337n23, 365–66, 395–97, 458, 526, 530–35, 537, 541, 545–46, 552n59, 567, 624n3, 677 Hommes, C. H., 16 Hong, James T., 291 Horneth, J. P., 646 Hortala-Vallve, Rafael, 413–14 Hortascu, A., 569 Hossain, Tanjim, 338n33, 618 Houser, Daniel, 118–19, 133n8, 138n71, 229, 276, 518 Hsu, M., 174–75 Hu, A., 625n29, 629n95 Huberman, Gur, 507, 510 Huck, Steffen, 110, 130–31, 138n66, 458 Huffman, David, 255 Hung, Angela, 404, 405 Husted, T. A., 13 Hyde, Janet S., 482, 483, 515 Iachini, M., 616–17 Ingram, P., 691 Iriberri, N., 590, 626n46 Isaac, R. Mark, 94, 98, 118, 124, 139n85, 295–98, 334–35nn5–7, 358, 565, 628n67, 685 Ivanov, A., 592 Ivanova-Stenzel, Radosveta, 574, 621

•

729

Jackson, M., 413 Jaing, J. H., 26–27 Jakiela, Pamela, 520 James, D., 565, 624n3, 628n67 Jeffrey, Scott A., 272 Jessup, R. K., 650 Jevons, William Stanley, 80n25 Jofre-Bonet, M., 628n72 John, E. R., 676 Kable, Joseph W., 181 Kagel, John H., 47, 49–50, 97, 137n53, 217, 226–27, 232, 242–43, 265, 275, 294–95, 306–7, 319–22, 369–74, 436, 438–43, 449–51, 464–65, 467–70, 511–12, 549nn23, 24, 563, 580–89, 592–601, 604, 607, 622, 627n65, 628n76, 686 Kahneman, Daniel, 127, 155, 173, 183, 647–48, 661, 662, 696 Kalandrakis, T., 374–76 Kariv, Shachar, 96, 119, 235–36, 520 Karlan, Dean S., 126–27, 179, 280n72 Karp, Richard M., 298 Kartal, M., 396 Kass, Norman, 527–28, 551n52 Katok, Elena, 100, 102, 135n26, 515, 568–69, 578–79, 606 Keane, M., 697 Keister, T., 24–25 Kelley, Harold H., 679 Kelling, G., 692 Kerschbamer, Rudolf, 548n14 Keser, Claudia, 134n25, 576–77 Kessler, Judd, 116, 137n57, 140n96, 332–33 Keynes, John Maynard, 19, 80n25, 81n36 Keysers, C., 199 Kim, Chung, 288 Kim, J., 571–72, 625n20 King-Casas, B., 196 Kinross, S., 604 Kirchkamp, O., 34, 37–38, 73–74 Kirchsteiger, Georg, 49, 234, 275, 276, 277n9 Kirkwood, Nicole, 254 Kiyotaki, N., 39, 41 Klemperer, Paul, 301, 417, 588, 610, 623 Klinowski, David, 136n42 Knetch, Jack L., 127 Knez, Marc, 138n73 Knoch, Daria, 187, 198 Knox, G., 665 Kogut, Carl, 440–42 Komai, Mana, 113–14 Kong, Fanmin, 518 Konrad, Kai A., 135nn30, 34 Koopmans, T. C., 4 Korenok, O., 18, 72–73 Kormendi, Roger, 357 Kosfeld, Michael, 261 Kosmopoulou, G., 628n72

730

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Name Index Kotchen, Matthew J., 135n27 Kovalchik, Stephanie, 452, 469, 471 Kranton, Rachel E., 253 Krause, Kate, 444–49, 469–71, 473n17, 539 Krekelberg, Bart, 167 Krishna, V., 610 Kröger, Sabine, 455–57, 470, 471 Kruse, J. B., 534 Kuang, Jason Xi, 104–5, 246–47, 275 Kube, S., 268–69, 271–73 Kuhnen, Camelia M., 502 Kume, Koichi, 452–53 Kumru, Cagri S., 117 Kuo, W. J., 191, 199 Kurzban, Robert, 118–19, 133n8, 138n71 Kwasnica, A. M., 611–13 Kwerel, Evan, 302, 305–6, 336nn15, 20 Lagos, R., 41, 43 Laibson, David, 13, 153, 183 Lakshminarayanan, Venkat, 173, 442–43, 469 Landa, Dmitri, 405 Landry, Craig E., 132 Lange, Andreas, 121–23 Laury, Susan K., 14, 98, 133n7, 135n29, 458, 526, 530–35, 537, 541, 545–46, 552n59, 624n3 Lavy, Victor, 503–4 Lazear, Edward P., 279n56 Lebiere, C., 667, 672 Ledyard, John O., 92, 133n2, 279n41, 299, 301, 470, 520 Lee, Soohyung, 328–29, 338n49 Lee, Y-J., 81n35 Lehrer, Steven F., 369–70, 580–81 Lei, V., 9–11, 21–22, 80nn10, 21 Leibbrandt, Andreas, 493, 504 Leider, Stephen, 258 Lejarraga, T., 650 Le Mens, G., 697 Lemieux, T., 698 Leonard, Kenneth L., 495 Lerch, J. F., 667, 672 Leufkens, K., 609 Levin, Dan, 294–95, 464–65, 467–68, 547n1, 563, 572, 583–92, 596, 598–601, 603–4, 606, 619–20, 625n51 Levin, I. P., 534 Levine, David, 393–96 Levine, Michael, 362–65 Levinthal, D. A., 674 Levitt, Steven D., 257–58, 465, 466 Levy, H., 534 Levy, Ifat, 163 Levy, Jonathan, 302, 305–6 Li, Sherry Xin, 254–55, 613 Lian, P., 56–57, 73, 81n42 Lichtenstein, Sarah, 526 Liday, Steven G., Jr., 446–47, 470

Lieberman, Matthew D., 185 Lien, Yuanchuan, 306–7, 607, 628n76 Lightle, John, 280n76 Lim, S., 2, 36–37 Linardi, Sera, 135n31 Lindsay, Luke, 299–300 Lipman, Barton L., 111, 136n47 List, John A., 106–8, 110–12, 121–23, 126–28, 136nn46, 49, 237, 245, 257–58, 267–68, 447–48, 464–70, 493, 495, 504, 596–97, 602–4 Liu, Thomas T., 167 Livne-Tarandach, R., 701n4 Llorente-Saguer, Aniol, 30, 413–17 Loewenstein, George, 131, 179 Loewenstein, Y., 667 Logue, A. W., 180 Lohrenz, T., 193 Lombardelli, C., 68 Lonnqvist, Jan-Erik, 543 Lopomo, G., 611 Lucas, R. E., Jr., 2–3, 8, 14, 21 Lucking-Reiley, David, 110–12, 136n46, 467, 602–3, 617 Luhan, W. J., 59–60 Lukas, Indra, 129–30 Lupia, A., 361, 422n68 Luria, A., 696 Luria, G., 692 Luthans, P., 696 Lynn, Michael, 519–20 MacDonald, Don, 441–42, 648 MacLeod, W. B., 698 Madiés, P., 26 Malach, Rafael, 167 Malmendier, Ulrike, 107–8, 179, 279n56 Malouf, M. W. K., 8 Mane, A. M., 695 Manelli, A. M., 628n66 Mankiw, N. G., 72 March, J. G., 663, 674 Marchiori, D., 662 Maréchal, M. A., 268–69, 271–72 Marimon, R., 15–16, 28, 34, 36–37, 81n34 Markovits, Daniel, 96, 235–36 Marks, Melanie, 254 Marschak, Jacob, 449, 565 Martin, C., 189 Martin, Richard, 115 Marx, Leslie M., 118–19, 139n74 Masters, William A., 490 Matheny, K. J., 7, 21 Matthews, Peter Hans, 125, 126 Matthews, Steven A., 118–19, 139n74 Maynes, Elizabeth, 464 Mayr, Ulrich, 103, 184–85, 490, 492–93 Mazur, J., 671 McAfee, R. Preston, 294, 300, 576, 619

Name Index McCabe, K., 33–35, 105, 190, 240, 260, 513 McClure, Samuel M., 155, 180, 198 McConnell, Margaret A., 135n31 McFadden, D. L., 660 McGee, P., 572, 686 McIntosh, C., 570 McIntyre, Frank, 500–501 McKay, Charles, 80n25 McKelvey, Richard D., 357, 359, 361, 364, 365, 368–70, 381, 383–86, 394, 401, 402, 404, 415, 422n64, 684 McKinney, C. Nicholas, 322–23 McManus, Brian, 123, 124, 139n87 McMillan, John, 300, 301, 619 Meidinger, Claude, 114 Meier, Stephan, 105–6, 115–16, 127–28, 132, 140n96, 255–56, 455–56, 473n25 Meissner, T., 6–7 Mengel, Friederike, 277n19 Menietti, Michael, 112, 132, 133n7 Menkhaus, D. J., 611 Menzies, G. D., 55 Merlo, A., 677 Merlob, Brian, 317–18 Meyer, R. J., 665 Miles, C. G., 450 Milgrom, Paul, 301–2, 306–7, 336n16, 511, 607, 628n76 Miller, David C., 528, 533, 535, 551n51 Miller, Gary, 357–58, 360–61, 368 Miller, John H., 95–96, 229, 235, 275, 278n33, 686 Miller, Luis M., 459–60, 470 Miller, N. F., 676 Millimet, Daniel L., 447–48, 469 Millner, Edward L., 128–29 Mischel, Walter, 179 Moaz, Zeev, 389 Montague, P. Read, 196 Montero, Maria, 243–44 Montmarquette, C., 607–8 Moore, E., 534 Morelli, Massimo, 132, 242–43, 370–74, 396 Morgan, John, 67–69, 119–23, 628n67 Morgenstern, Oskar, 137n51 Morin, Louis-Philippe, 503 Morris, S., 30, 31 Morton, Rebecca, 79n3, 372, 389–90, 405, 407–9 Moser, D., 49–50, 232, 265 Moulin, H., 19 Moxnes, Erling, 116 Müller, Julia, 489–90, 494 Müller, Wieland, 458 Muren, Astri, 517–18 Murphy, Kevin M., 201n5 Muth, J. F., 14 Myers, Caitlin Knowles, 140n96, 457, 460 Myers, J., 643–44

•

731

Myerson, E., 564, 575 Myerson, Roger, 387, 388, 417 Myung, I. J., 673 Naef, Michael, 232 Nagel, R., 19–20, 31–32, 77, 190–92, 198, 413–14, 457–58, 471 Nagel, Thomas, 133n5 Nash, John, 290, 701n1 Neiman, T., 667 Nelson, Julie A., 552n58 Nettle, Daniel, 135n33 Neugebauer, T., 566–68, 577 Nevo, I., 647–48, 655, 657–58, 663–64, 699 Niederle, Muriel, 228–29, 322–29, 391, 485–91, 495–99, 502–4, 507–10, 516, 536, 543, 545, 547, 548n12, 592 Nieken, Petra, 501 Niemi, Richard, 361, 364 Nikiforakis, Nikos, 256 Niskanan, William A., Jr., 359 Noe, T. H., 610 Noor, Jawwad, 136n38 Normann, Hans-Theo, 244 Nosenzo, Daniele, 138n66 Noussair, C. N., 5, 7, 9–11, 21–22, 38, 50–53, 57–59, 73, 74, 80nn10, 21 Nunnari, Salvatore, 378–81 Nystedt, Paul, 454, 456, 471 Obama, Barack, 520 Oberholzer-Gee, Felix, 244–45, 276 Ochs, J., 15, 32, 34, 39–41, 81n32, 118–19, 221–22, 681 Ockenfels, Axel, 217, 219, 222–26, 229–32, 265, 280n63, 308–16, 337n26, 338n34, 446, 617–18, 624n6 Ockenfels, P., 31–32 O’Doherty, J., 194–95, 198 O’Donoghue, T., 13, 519–20 Offerman, T., 13, 76–77, 81n51, 134n22, 282n96, 575, 593, 613–16, 622–23, 625n29 Olson, Mark, 299, 576–77 Onderstal, Sander, 125, 135n34, 139nn79, 82, 625n29 O’Neill, B., 682 Oosterbeek, Hessel, 504, 507, 510, 536 Oprea, Ryan, 138n69 Ordeshook, Peter C., 357, 359, 381, 383–86, 415, 422n64 Orland, A., 73 Ors, Evren, 503 Ortmann, A., 24 Orzen, Henrik, 121–22, 124–25 Ostrom, Elinor, 92 Ostrovsky, Michael, 338n54 Ottoni-Wilhelm, Mark, 102–4

732

•

Name Index Overmeier, J. B., 674 Ozbay, E. Y., 568–69, 624n10

Putterman, Louis, 518 Puzzello, D., 34, 42, 43

Palacios-Huerta, Ignacio, 465, 466 Palfrey, Thomas R., 98, 99, 347, 365, 374–76, 378–81, 387, 391–96, 401, 402, 404, 405, 407–12, 415–17, 567, 620–21 Palomino, Frédéric, 503 Palumbo, M. G., 8–9 Pande, Rohini, 548n4 Parkhurst, G. M., 570 Paruolo, P., 73–74 Pate, Jennifer, 548n12 Pavlov, Ivan Petrovich, 675 Pearson, M., 193 Peeters, R., 609 Pekec, Aleksandar, 303 Peranson, E., 322 Pesendorfer, M., 628n72 Pesendorfer, Wolfgang, 401, 402, 407 Peter, T. L., 139n87 Peters, H. Elizabeth, 445, 473n14 Petersen, L., 44–45 Pevnitskaya, Svetlana, 124, 620–22, 684 Peyrache, Eloïc, 503 Pezanis-Christou, P., 573–74, 577 Pfajfar, D., 70–71 Phelps, E. S., 67, 182 Phelps, Michael E., 164 Phillips, A. W., 2 Phillips, O. R., 611 Pitchik, C., 628n71 Platt, M. L., 193, 194 Plonsky, O., 655, 672 Plott, Charles R., 2, 50–53, 55–59, 73, 81n42, 291, 295–98, 300–301, 317–18, 334–335nn5–7, 349, 352–58, 362–65, 382, 389–90, 404–5, 469–70, 474n54, 613, 628n78 Poen, Eva, 521–22 Pogrebna, G., 116 Pollack, R. A., 182 Pope, Devin G., 468 Popkowski, Leszczyc, 139n87 Porter, D., 35, 299, 301, 601–2 Potters, Jan, 76–77, 112–14, 117, 535, 541, 613–14 Poulsen, Anders, 497 Powell, Melanie, 534 Prasnikar, Vesna, 276, 278n36 Prelec, D., 175, 671 Prescott, E. C., 2, 36–37 Price, Curtis R., 490 Price, Joseph, 500–501 Price, Michael K., 121–23 Prisbrey, Jeffrey E., 98–100 Proctor, Deborah D., 326 Proudman, J., 68 Puppe, C., 268–69, 271–72

Rabin, M., 13, 218, 219, 222, 230–31, 233–34, 243–44, 275–76, 278n28, 526, 567–68 Ramsey, F. P., 4 Rand, David G., 521 Randal, John, 115 Rangel, Antonio, 181, 198 Rao, Justin, 135n31 Rapoport, Amnon, 137nn50, 51, 389, 680, 683–85, 687 Rapoport, Anatol, 520 Rassenti, Stephen J., 297–98, 335n8, 336n16 Rasul, Imran, 130–31 Razzolini, L., 565–66 Read, Daniel, 179 Rebello, M. J., 610 Recalde, Maria, 133n7, 136n38, 460, 513 Rege, Mari, 105 Reidl, A., 74–75 Reiley, David H., 465, 603–4 Reilly, Robert, 128–29 Reis, R., 72 Reiskamp, J., 673 Reiss, J. P., 608–9, 628n72 Reizman, R. G., 50–53, 57–59 Ren, Linxia, 136n38 Renner, Elke, 116 Rescorla, R. A., 675–76 Reuben, Ernesto, 506 Rey-Biel, Pedro, 110, 138n66, 549n22 Reynolds, Morgan O., 450–51, 469 Ricciuti, R., 63 Richard, J. F., 583–86, 592–93 Riedl, Arno, 133n7, 136n38, 275, 276, 460, 513 Riener, Gerhard, 491, 497 Rietz, Thomas, 388, 389–90 Riezman, Raymond, 412 Rigotti, L., 254 Riker, William H., 414–15 Riley, J. G., 564 Rilling, J. K., 184 Rischall, Isaac, 520 Rivas, Maria Fernanda, 116, 118 Robert, J., 607–8 Roberts, Gilbert, 135n33 Roberts, John, 511 Rockenbach, Bettina, 270–71, 465 Rodensky, D., 690–91, 693 Rodriguez, Monica Larrea, 179 Rodriguez-Mora, J. V., 32, 77 Roiser, J. P., 201n7 Romano, Richard, 110–11, 116–17 Romer, Thomas, 359–60, 366–68 Rondeau, Daniel, 127, 136n49 Roopnarine, Anil, 336n16 Roos, M. W. M., 27, 59–60, 73

Name Index Rose, S. L., 589 Rose-Ackerman, Susan, 136n44 Rosenthal, Howard, 359–60, 366–68, 392–93 Rosenthal, R., 474n37, 682 Rotemberg, Julio J., 224, 281n96 Roth, Alvin E., 8, 218, 221–22, 227, 236–38, 276, 277n2, 278n36, 290, 308–13, 318–29, 335nn8, 9, 337n26, 338nn45, 55, 470, 484, 606, 617–18, 660, 677–78, 681, 686, 687 Rothkopf, Michael H., 139n87, 293, 303 Roy, C. S., 164 Rubinstein, Ariel, 507, 510 Rustichini, Aldo, 219, 254, 264, 391, 497–500, 502–3, 507, 545 Rützler, Daniela, 279n42 Sade, O., 611 Sadler, E., 643–44 Sadrieh, Abdolkarim, 270–71 Salant, S. W., 358 Salmon, Timothy C., 124, 139n85, 577, 616–18, 621 Samuelson, Larry, 138n67, 236–38 Samuelson, W. F., 294, 564 Sandberg, Sheryl, 481, 484 Sandholm, T., 335n9 Sanfey, Alan G., 196 Santos, Laurie R., 173, 442–43, 469 Sapienza, Paola, 257–58 Sargent, T. J., 2, 65–67, 81n45 Satpute, Ajay B., 185 Satterthwaite, M., 417 Savage, L. J., 696 Schafer, William D., 528, 533, 535, 551n51 Schelling, Thomas C., 108, 118, 131, 138n67 Schenck-Hoppe, K. R., 35–36 Schiff, Jerald, 136n44 Schlag, Karl, 677 Schmidt, Klaus M., 217, 222–25, 229, 231–32, 244, 275–76, 446, 457, 461 Schmittberger, K., 687–88 Schmittberger, Rolf, 513 Schnier, Kurt, 124 Schnitzlein, C., 611 Schooler, L. J., 670 Schotter, A., 25–26, 46, 178, 391, 615–16, 628n71, 677 Schram, Arthur, 125, 134n22, 135n34, 139nn79, 83, 392–93, 396–98, 422n84, 622–23 Schubert, Renate, 530, 532, 534 Schunk, Daniel, 518 Schwarz, Michael, 338n54 Schwarze, Bernd, 513, 687–88 Schweitzer, Maurice E., 468 Schwieren, Christiane, 489–90, 494 Sefton, Martin, 112–13, 117, 120–22, 138n66, 628n66 Segal, Carmit, 495–96, 548n12

•

733

Seki, Erika, 256, 464, 470 Seligman, M. E. P., 674 Sell, Jane, 254 Selten, R., 457–58, 471, 566–68, 624n6, 685–86 Semmelweis, Ignaz, 693, 702n16 Servátka, Maroš, 491, 495 Shachat, J. M., 683 Shafir, E., 43, 128 Shafir, S., 648–49, 651 Shahriar, Q., 618–19 Shaked, Avner, 224–25 Shang, Jen, 115, 132 Shearer, Bruce, 270, 281n91 Shell, K., 27 Sheremeta, Roman M., 490 Sherrington, C. S., 164 Sherstyuk, K., 611–13 Shi, Y., 665 Shiller, R. J., 81n36 Shin, H.-S., 30, 31 Shoda, Yuichi, 179 Shogren, Jason F., 280n58, 570 Shteingart, H., 667 Shum, M., 697 Shurchkov, Olga, 501 Sidowski, J. B., 677 Siegel, D., 695 Siegel, Sidney, 462, 470 Silvestre, J., 59–60 Simons, Daniel J., 547n1 Sims, C. A., 78 Sirigu, A., 193 Skinner, B. F., 672, 688–89, 696 Skogan, W. G., 692 Slonim, Robert, 218, 256, 258, 448, 470, 473n16 Slovic, Paul, 131, 526, 528, 538–40, 551n46 Small, Deborah A., 131 Smalley, W., 693 Smith, Adam, 181 Smith, J., 619–20 Smith, T. G., 676 Smith, Vernon L., 2, 105, 291, 297–98, 301–2, 336n16, 701n2 Snyder, Jessica, 254 Soetevent, Adriaan R., 114–15, 135n34 Solomon, R. L., 675–76 Solow, John L., 254 Solow, R. M., 49 Song, Fei, 491, 495 Sönmez, Tayfun, 330 Sonnemans, Joep, 134n22, 392–93, 396–97 Sonnenschein, H., 413 Sonsimo, D., 687–88, 696 Stajkovic, A., 696 Stanca, Luca, 125, 140n91 Stegeman, Mark, 113–14 Sternberg, Saul, 166 Stockman, Carol, 238–39

734

•

Name Index Stoecker, R., 685–86 Stout, J. C., 657 Strobel, Martin, 231, 232 Strotz, Robert Henry, 182 Sugden, Robert, 110 Sullivan, H., 628n78 Sunder, S., 2, 15–16, 28, 34, 36–37 Sunstein, Cass R., 126, 130 Suppes, P., 680–81 Susuki, Ayako, 452–53 Sutter, Matthias, 116, 118, 134n25, 279n42, 446, 457, 461, 493, 496–97, 548n14 Svenson, L. E. O., 69 Swanson, Joseph A., 299 Swineford, Frances, 527, 550nn41, 42 Szkup, M., 32 Tabibnia, Golnaz, 185 Tabory, L., 677 Tajfel, H., 253–54 Takahashi, Hidehiko, 175 Takeuchi, K., 605 Talbot, J., 68 Taleb, N. N., 699 Tannenbaum, Daniel I., 545 Tasnádi, A., 676 Tavits, Margit, 397 Taylor, J., 69–70, 71 Taylor, Laura O., 135n29 Telle, Kjetil, 105 Teoderescu, K., 655, 672, 674–75 Terkel, J., 676 Terracol, Antoine, 466–67 Teyssier, Sabrina, 548n13 Thaler, Richard H., 126, 130, 132, 457 Thevarajah, D., 194 Thibaut, J. W., 679 Thomas, Susan H., 94 Thompson, M. A., 534 Thöni, Christian, 474n33, 523 Thorndike, E. L., 642, 656, 671 Tirole, Jean, 105, 135n30 Titmuss, Richard M., 140n96 Tobin, Henry, 180 Tobler, P. N., 175 Tolman, E. C., 670 Tom, S. M., 173, 201n8 Torma, David P., 299 Townsend, J. T., 643 Tractman, Hannah, 135n31 Treich, N., 566 Trevino, I., 32 Tricomi, Elizabeth, 184–85 Tucker, S., 38 Tullock, Gordon, 398, 414 Turban, Sebastien, 417 Turdaliev, N., 68–70 Turner, J. C., 253–54

Tversky, Amos, 43, 173, 647–48, 661, 662, 696 Tymula, Agnieszka, 502 Tyran, Jean-Robert, 43–45, 399, 408 Uecker, Wilfred C., 462, 464 Ule, A., 13 Ünver, Utku, 330, 335n9 van Damme, E., 30, 80n27, 225 Van der Heijden, E. C. M., 74–75, 116 Van Huyck, J. B., 64–65 Van Leeuwan, Barbara, 179 van Soest, Arthur, 456–57, 459, 470 van Winden, F., 74–75 Varian, Hal R., 93, 109, 110, 136n42, 338n54, 451 Vaughan, W., Jr., 671 Verbon, H. A. A., 76–77 Vesterlund, Lise, 92, 102–4, 109–13, 117–19, 132, 133n7, 134n16, 135n34, 136nn38, 42, 137n58, 277n12, 445–49, 460, 469, 471, 473n17, 485–91, 495–96, 502–3, 513, 516–19, 523, 525, 539, 543, 545, 547, 548n12 Vickrey, W., 467, 599, 602–5, 627n64, 628n66 Villeval, Marie-Claire, 114, 117–18, 453, 470, 494, 497, 548n13 Vincent, D., 576 Viscusi, W. K., 649 Vogt, B., 35–36 Volden, C., 372 Volij, Oscar, 465 von Gaudecker, Hans-Martin, 459 Von Neumann, John, 137n51 Vorsatz, V., 609 Vragov, R., 601–2 Vul, Edward, 201n8 Wakker, P., 661 Walker, James M., 94, 98, 118, 570–71, 685 Wallis, W. Allen, 230 Walters, M. F., 64–65 Wan, Zhixi, 579 Warwick, P. V., 372 Weber, Elke U., 540, 651 Weber, Robert, 387, 388 Weber, Roberto A., 104–5, 138n73, 246–47, 275, 279n56 Weck-Hannemann, Hannelore, 134n25 Wegner, D., 662 Weigelt, Keith, 391 Weil, M., 695 Weingart, Laurie, 523, 525 Weimann, J., 231 Wengström, Erik, 459 Whinston, M. D., 614 Wik, M., 536 Wilcox, N. T., 8–9 Williams, Arlington W., 98 Williams, Kenneth C., 79n3, 384, 386, 405

Name Index Williams, Melonie B., 458 Wilner, B. S., 628n66 Wilson, B. J., 81n47, 577, 618 Wilson, B. R., 587 Wilson, J. Q., 692 Wilson, Rick K., 254, 357, 365, 420n24 Wilson, Robert B., 292, 293, 301 Winn, A., 44–45 Wiseman, A., 372 Wiswall, Matthew, 506 Wolfe, Katherine, 226–27, 275 Wolfstetter, E., 574 Wooders, J., 465, 570–71, 618–19 Woolley, H. T., 483 Wozniak, David, 490, 492 Wright, R., 39, 41, 43 Wu, S. W., 175 Wykoff, L. B., 677 Xi, H., 81n35 Xiao, Erte, 229, 276 Xie, Huan, 102–3, 104 Xu, Y., 26–27 Yang, C.-L., 231 Yariv, Leeat, 404–5

•

Ye, L., 622 Yechiam, E., 645–46, 649, 657, 665, 673, 693–95 Yestrumskas, Alexandra H., 508–10 Yildirim, Huseyin, 110–11, 116–17 Yin, Wesley, 179 Yorulmazer, T., 25–26 Yoshida, W., 192, 198 Yoshimoto, H., 625n12 Zafar, Basit, 506 Zakelj, B., 70–71 Zauberman, Gal, 178 Zeckhauser, Richard, 549n30 Zehnder, Christian, 255–56, 455–56, 473n25 Zeiler, Kathryn, 469, 470, 474n54 Zender, J. F., 611 Zhang, Y. Jane, 506 Zhang, Yuanjun, 317–18 Ziller, Robert C., 542 Zimbardo, P. G., 692 Zingales, Luigi, 257–58 Zizzo, D. J., 55 Zohar, D., 692 Zsiros, J., 73 Zwick, Rami, 249, 277n11

735

SUBJECT INDEX addiction, 201n5 affirmative action, 495–96, 502, 549n22 age, 186, 279n42, 492–94. See also children; elderly agendas. See committee bargaining airport takeoff and landing slot allocation, 295–300, 335nn10 and11, 336n15 Allais paradox, 441, 443, 458, 469, 647–48 altruism, 100–104; and age of subjects, 279n42; and charitable giving, 93–94, 97–104, 109, 134nn16 and18, 135n23; and children, 444–45, 518; and committee bargaining, 358; and crowding out of individual contributions to public goods, 100–103; defined, 133n5; and dictator game, 224, 258; “directed” altruism, 258; directions for future research, 523; and gender, 483, 487, 512–25, 549n25; impure altruism, 97, 99, 102–4, 134n18, 135n28; and neurobiology, 103–4, 186; price of giving, 126–31, 186, 483, 524, 549n27; pure altruism, 97, 99, 100, 134n16; and sequential giving, 109; warm-glow altruism, 97–104, 134nn18, 22 and 25, 183 Amazon.com auctions, 308–13, 617–18 amygdala, 162, 164, 166, 173, 176, 177, 195, 201n7 animal subjects, 437–44; consumption choice and labor-leisure experiments, 47, 440–41; and delayed gratification, 180, 442; and GARP, 439–40, 442–43, 469; and hyperbolic discounting, 470; and learning, 443–44, 642, 646, 648–49, 668–71, 674–75; methodological considerations, 438–39, 443–44; and rational choice theory, 438; and risky choice studies, 441–43; and strategic thinking, 189, 190, 194 anterior cingulate cortex (ACC), 174, 186 auctions, 564–629; and advantaged bidder, 588–89; all-pay auction, 124–26, 140n91; Amazon.com auctions, 308–13, 617–18; Amsterdam auction, 575, 625nn27 and 29; auctions with both common and private value elements, 593; auctions with synergies, 605–7; Ausubel auction, 599, 602, 604, 627n65, 628n66; bidder’s choice auctions, 615–17; buyer-determined vs. price-determined mechanism, 578–80; cash-balance effects and role of outside earnings on bids, 580–81; charity auctions, 108, 123–26, 139–40nn83–88, 91; charity vs. noncharity auctions, 123–24, 139–40n87; and collusion among bidders, 610–15; combinatorial auctions, 300–303, 306–7, 335n9, 607; common value auctions,

292–95, 408–9, 582–98, 626n46; compared to lotteries, 123–25, 139n83; compared to voluntary contribution mechanism, 124–25; and crowding out intrinsic motive for giving, 126; and demand reduction, 598–604; directions for future research, 569; double-auction experiments, 3, 28–29, 35–36, 49, 57, 259–60, 299–300, 335n7, 571; Dutch auction, 564–65, 608, 624n1; eBay auctions, 307–16, 337nn27–30, 338nn33–37, 617–18; English/ascending auction, 123, 564–65, 579, 583, 608, 624n1, 626n36; English clock auction, 575, 577, 583–87, 589, 598–601, 604, 618–19; “entirety bidding,” 299; entry into auctions, 619–23; excluded-bid auction, 317–18; field studies, 126, 569; first-price auction, 124, 139n83, 293–94, 409, 564–67, 584–86, 622–23, 624n1; good-by-good auctions, 615–16; and insider information, 587–88; jump bidding, 626n36; and learning, 313; methodological issues, 581–82; multiunit-demand auctions, 598–609, 613, 621–22; and oil industry, 582, 597; package bidding, 297–307, 330, 336n18, 337nn23–25, 604–7; participation rates, 125; private-value auctions, 124, 564–82; procurement auctions, 316–18, 578–80; and professionals/experienced bidders, 461–63, 467, 570–71, 592–93, 625–26n31; radio spectrum auctions, 294–95, 300–307, 588–90, 598, 605; regret theory, 568–69, 624n10, 625n12; and revenue equivalence theorem (RET), 564; and risk preferences, 565, 624nn3 and 4, 625n12; sealed-bid auctions, 293–94, 309–10, 584–86, 598–601, 622–23; second-price auction, 125, 309–12, 459, 564–65, 570–72, 624n1; selection bias, demographics, and ability effects, 593–95; sequential auctions, 576–78, 607–9, 611; silent auctions, 123, 140n88; simultaneous ascending auctions, 300–301, 306–7, 607, 611–13, 622–23; sophisticated bidding, 590; and subject populations, 570–71, 592–93, 611, 625–26n31; survivor auction, 627n65; takeover game, 590–92; uniform-price sealed-bid auction, 598–601; Vickrey auction, 467, 599, 602–4, 627n64, 628n66; wallet-game auction, 588–89; winner-pay auctions, 123–25; and winner’s curse, 292–95, 408–9, 468, 564, 582–83, 590–98, 619. See also market design experiments autism, 176, 190, 196 axiomatic social choice theory, 349–52, 400

738

•

Subject Index baby sitting (natural experiment), 35–36 bank runs, 24–27, 80n28 bargaining games, 195, 222, 242–44, 446–47. See also committee bargaining; dictator game; investment game; trust game; ultimatum game basal ganglia, 162–65 Battle of the Sexes, 684 beauty contest game, 19–20, 191–92, 458–60, 466, 471 belief: beliefs about others and strategic thinking, 190–92, 201n13; and choice of challenging tasks, 510; and competition, 486, 490, 502; and expectation formation, 14, 234; and other-regarding behavior, 222, 234–35, 277n9; and reciprocity, 234; and voter turnout, 397–98. See also expectations benzodiazepine, 188 best-shot game, 278n36 betting games, 687–88 blood donation, 281n86, 520 bluffing, 194, 195 bonds, 61–63 borderline personality disorder, 196 borrowing, 6–7, 59–60. See also credit brain: abnormalities, 154, 174, 176, 177, 187, 190, 196, 200, 656–57; brain stimulation experiments, 154, 175, 180, 181, 183, 188; cellular structure, 156–60; and competition, 492; and the elderly, 452; executive function/willpower studies (intertemporal choice and self-regulation), 178–83; and gender, 492; neuroimaging (see neuroimaging); pharmacological experiments, 188; social preferences studies, 183–89. See also cognition; neuroeconomics; strategic thinking studies; specific brain regions, such as prefrontal cortex brainstem, 162, 164 broken windows theory, 692 business-cycle theory, 4, 47 call market, and sunspot variables, 28–30 cannabis, and productivity, 450, 473n20 caudate, 104, 162–63, 184, 186, 191, 196 centipede game, 461, 466–67, 474n37 central banks, 36, 65–73 centrally planned economies, 463 cerebral cortex, 162–65, 168, 180. See also prefrontal cortex charitable giving, 91–140; and altruism, 93–94, 97–104, 109, 134nn16 and18, 135n23; charity debit card proposal, 126; and concern for others vs. concern for others’ inferences about oneself (image effects), 104–8, 135n33, 140n96; and crowding out intrinsic motive for giving, 97, 100–103, 126–28, 134nn24 and 25, 135n26, 140nn94 and 96; and decision errors, 97–99, 119, 133n8, 136n38; and delegation to nongenerous agent, 105, 135n32; and dictator

game, 94–96, 100–103, 105–7, 131, 133n6; free rider problem, 91, 93, 97, 109, 110, 133n8, 134n18; fundraising mechanisms, 108–33 (see also fundraising); and gender, 519–20; and moral wiggle room, 100, 105, 108, 135n31; motives for giving, 91, 95, 97–110, 114, 134nn16,18, 22, and 25, 135nn23 and 28, 140nn94 and 96; and neurobiology, 103–4, 135n28, 184, 187; and opting out, 105, 108, 135n31; preferences for specific charities, 102, 104, 135nn29 and 35; price of giving, 126–31, 483; rationality of giving, 95–96; and signaling, 95, 106–7, 135n30; signaling quality of charities, 110–17, 140nn87 and 94; and social distance, 105, 106, 108; and social norms/social pressure, 106–7, 116; standard voluntary public good model, 93–94; and taxes, 97; uncertainty in quality of charities, 136n44; and visibility, 105–6, 108, 115, 135n34; and voluntary contribution mechanism (VCM; linear public good game), 94–95, 105–6, 117–21, 133n8, 136n38, 138n71; and warm-glow giving, 97–104, 134nn18, 22 and 25 children, 437, 444–49, 470–71; and altruism, 444–45, 518; Becker’s Rotten Kid Theorem, 445; and competition, 493–94, 500–501; and delayed gratification, 180, 448–49; and endowment effect, 448, 469; and GARP, 447–48, 469; and group identity, 445; and hyperbolic discounting, 448, 470; and market experience, 447–48; methodological considerations, 449; and observational learning, 676–77; and other-regarding behavior, 279n42, 445–47, 470; and rational choice, 448–49; and risk preferences, 529, 542; and voluntary contribution mechanism (VCM; linear public good game), 470–71 choice prediction competitions, 665–68 clicking paradigm, 640–44, 646–49, 651–55, 659, 665–66, 669–75, 700 cobweb model, 16–19, 20 cognition: cognitive-hierarchy theories, 190–91; confusion and charitable giving decisions, 128–29, 133n8; and consumption/savings decisions, 9; depth of thinking, 190–92; and fundraising, 114, 128–29, 131; and identifiable victim, 131; and labor economics, 264–65; and learning, 640–41, 671, 673–74, 687; and other-regarding preferences, 264–65; and risk preferences, 264; and signaling, 114; and step-level reasoning, 19–20. See also expectations; learning; neuroeconomics; strategic thinking studies Cohen’s d, 514–15, 528–29, 536–37 college course allocation system (Wharton School), 329–33 commitment, demand for (savings accounts), 179, 182

Subject Index committee bargaining, 350–81, 420nn24–26; agenda-control experiments, 359–61; average-value decision rule, 364; avoid-the-worst decision rule, 364; Baron-Ferejohn bargaining model and experiments, 366–74; committee bargaining with fixed structure, 359–81; demand bargaining, 371–72; divide-the-dollar experiments, 351, 369–78; divide-the-question agenda, 362–63, 365; dynamic bargaining in the shadow of a voting rule, 366–81; dynamic legislative bargaining with durable public goods, 378–81; empty core experiments, 358–59; finite horizon experiments, 372; Gamson’s law, 370–71; legislative bargaining, 372–74; majority-rule core experiments, 353–57; robustness of core clustering, 357–58; Romer-Rosenthal monopoly agenda-setter model, 366–68; Rubinstein-Stahl bargaining game, 366–67; and sophisticated voting, 361–66; unstructured committee bargaining, 352–59; voting over fixed agendas, 361–66. See also jury trials committees, information aggregation in, 352, 400–410 communication: collusion in auctions, 610–15; and coordination problems, 136n43; freedom of expression and economic growth, 22–24; and jury trials, 402, 404–6; and trust game, 234–35; and voter turnout, 397–98. See also signaling comparative advantage, law of (international trade), 50–51, 55 competition: and age of subjects, 492–94; and beliefs, 486, 490, 502, 548n14; and the brain, 492; and children, 493–94, 500–501; and culture, 495; directions for future research, 494, 502; and education choices, 504–7, 510; and the elderly, 453; field studies, 503–4; and gender, 483, 485–507; gender differences in performance, 497–504, 549nn19–22; gender differences in tournament entry, 486–97, 548nn12–14; and high stakes, 486; and hormones, 492; and institutional design, 495–97; linking tournament entry and performance in tournaments, 502–3; and other-regarding preferences, 487; and personality, 494; and priming, 495; and risk aversion, 486–87, 490–91; and role of the task, 491–92, 501; and socio-economic status, 494 Condorcet jury problem, 352, 400–406 Condorcet winners, 350, 351, 365, 381–83, 386 conflicts, interpersonal, 698–99 constant sum games, 680–82 consumption and savings decisions, 4–14, 22, 28, 35, 37–38, 179, 439–40 contagion (bank runs), 27 cooperation: and the elderly, 453; free riders, conditional cooperators, and unconditional

•

739

cooperators, 257; and gender, 512–25; and social interaction and learning in games, 683–87; social preferences and reward circuitry, 183. See also social preferences coordination problems, 2, 21–32; bank runs, 24–27; and communication, 136n43; and elections, 382–84, 388–90; and fundraising (sequential giving), 111–12, 136n43; global game approach, 30–32; and leadership, 136n43; poverty traps, 21–24, 27; and role of institutions (freedom of expression and voting) in economic growth, 22–24; and social interaction and learning in games, 683–87; and sunspot variables, 27–30, 80n25; and voting behavior, 393, 422n79 credit, 59–60 crime rate, 692 currency markets, 51–55. See also monetary economics debt, 7, 61–63 decisions from experience, 638–68; and choice prediction competitions, 665–68; vs. decisions from description, 638–40, 647–51, 661–63, 698–700; and enforcement of safety rules, 689–91; and hand washing, 692–93; individual differences, 656–57, 659; inertia and surprise-triggers-change, 655–56, 658–59; and interpersonal conflicts, 698–99; and Iowa gambling task, 656–57; and I-SAW model, 657–61, 665–66; and limited feedback, 663–67; and observational learning, 677; properties of, 641–68; and rare events, 647–51, 661–62, 699–700; and reinforcement learning and fictitious play, 659–61; and safety devices and buying-using gap, 693–94; and timing of warnings, 693; very recent and wavy recent effects, 651–55, 658 decision utility, defined, 183. See also revealed preferences delayed gratification, 178–83, 442, 448–49. See also executive function deposit insurance, 24–26 dictator game, 219–20, 276, 279n42, 280n58; and altruism, 224, 258; and charitable giving, 94–96, 100–103, 105–8, 133n6; and children, 446–47, 518; compared to ultimatum game, 219–20; concerns about robustness, 244–47, 276; critical papers listed, 275–76; and crowding out of individual contributions to public goods, 100–103; and delegation/diffusion of responsibility in laying off workers, 249–53; and demand-induced effects, 245–47; described, 219–20; and gender, 513, 515–19, 524; and group identity, 254–55; and identifiable victim, 131; and lotteries, 244–45, 247; and models of other-regarding preferences, 224–25, 230; multiple-dictator games, 249–53;

740

•

Subject Index dictator game (continued) and opting out, 105, 247, 279n56; peasant-dictator game (monetary policy), 64–65; and perception of actions by self and others, 275; and personality, 264; and rational choice theory, 235–36; and rationality of giving, 95–96; and representative sample, 456–57, 460; and social norms, 106–7, 225; and subject populations, 470; three-person games, 236; two-step binary game, 246–47; utility function, 224–25 discounting, 2; and children, 448; and consumption/savings decisions, 5, 12–14; exponential discounting and infinite horizons, 12–13; exponential or hyperbolic discounting, 13–14, 448, 470; and intertemporal choice and self-regulation, 178–81; and money-time choices, 13–14, 178–79; and multiple-self and unitary-self models, 182–83; present bias, 182; and subject populations, 470 doctors, and labor markets, 318–26 dominance-solvable matrix games, 191 donation boxes (field studies), 115 dopamine, 162, 163, 175, 180, 194, 659 dynamic giving (fundraising technique), 118–19, 138nn67, 69, 70, 71, and 73, 139n74 eBay auctions, 307–16, 337nn27–30, 338nn33–37, 617–18; buy-it-now option, 618–19; charity vs. noncharity auctions, 139–40n87; reputation system, 313–16, 338nn36 and 37; second-chance offers, 618; sniping vs. squatting, 618 education, 460, 469; gender, competitiveness, and education choices, 504–7, 510; and negative effects of punishment, 688–89; and strategic thinking, 454 efficiency: efficiency vs. equity trade-off, 231–32, 518–19, 524; and gender, 518–20, 524; and other-regarding preferences, 217 efficiency wage theory, 47–50, 260 elderly, 75–77, 437, 451–56, 461, 542 elections and candidate competition, 351–52, 381–91, 397; alternative voting procedures, 388, 390, 422n74; and campaign contributions, 388–90; Condorcet winners, 350, 381–83, 386; convergence of candidate platforms, 381–87; effect of candidate quality on candidate divergence, 352, 390–91, 422n77; median voter theorem, 352, 385; multicandidate elections, 387–90; polls and information aggregation, 352, 381–84, 388, 390, 397–98; retrospective voting, 352, 381, 384–87, 390; two-candidate elections with majority rule core, 381–82. See also voting emotion, 183–86, 229, 278n29, 676. See also hedonic states; neuroeconomics endowment effect, 448, 452, 458, 467, 469–70 exams: cheating, 691–92, 702n15; and gender, 482, 543–45. See also SAT scores exchange-rate determination, 45, 51–55, 59

executive function, 178–83 exercise, optimism about future commitment to, 179 expectations, 2, 14–20; adaptive expectations and monetary policies, 65–67; and beauty contest game, 19–20; and beliefs about others, 14, 234; and bounded rationality, 16; and fiscal policies, 73–74; and inflation forecasting, 37–38, 65–67, 71; and price forecasting, 15–20. See also belief; rational expectations expected utility: and animal subjects, 441–42; and decisions from description, 639; and gender, 483, 526; and neural activation, 160, 161, 172; and prospect theory, 172; and reversed certainty effect, 648; and risk aversion in auctions, 568; and subject populations, 469 eye-tracking studies, 190, 199–200 fairness, 219–21, 224–25, 687–88; and committee bargaining, 358, 369; and delegation/diffusion of responsibility, 249–53; dissociation between fairness judgments and fairness behavior, 187; and learning, 687–89; and neurobiology, 184, 186–88; procedural fairness, 247–49; punishing unfair behavior, 184, 220–21, 229; and three-player sequential step-level public goods game, 239. See also dictator game; inequality aversion; intentionality; reciprocity; ultimatum game FCC spectrum auctions, 294–95, 300–307, 335n9, 336n18, 337n23, 588–90, 598, 605 financial crises, 80nn25 and 28. See also bank runs financial decisions, 699. See also consumption and savings decisions; debt; investment fiscal and tax policies, 73–78 forecasting, 2, 71; inflation forecasting, 37–38, 65–67; learning-to-forecast experimental design, 15–18, 37–38; price forecasting, 15–20 free rider problem, 91, 93, 97, 109, 110, 133n8, 134n18, 257, 303, 305, 392 functional MRI (fMRI), 153, 164–77, 183–85, 188, 191, 194, 196, 199–200, 201nn7 and 8; and experimental design considerations, 166–68; image analysis, 168–72; and risky choice studies, 172–77 fundraising, 91, 108–33; all-or-nothing strategy, 131–32; auctions, 108, 123–26, 139–40nn83–88; contribution maximization as objective, 92, 109, 136n39; and crowding out of intrinsic motive for giving, 127–28; door-to-door fundraising, 107, 126, 267; dynamic giving, 118–19, 138nn67, 69, 70, 71, and 73, 139n74; field studies, 107, 114–16, 122, 126–27, 130–32, 136n46, 137n56; and fixed costs of production, 110; free rider problem, 109, 110; and gift exchange, 132; and identifiable victim, 131, 140n103; isolation effect, 129, 130; and lead donor, 113–14, 116–17, 131; lotteries/raffles, 92,

Subject Index 108, 119–23, 139nn75–78 and 83, 140n96; matched contributions and rebates, 92, 108, 126–31, 140nn94 and 100; and price of giving, 126–31; and reciprocity, 114; refunds, 111, 112, 136n47; and response time, 136n38; seed donations, 111, 115, 131, 140n94; sequential vs. simultaneous contributions, 109–18, 136nn40, 42, 43, 45, 46, and 49, 137n50, 138n66; shortand long-term consequences of fundraising format, 127–28, 132; signaling quality of charities, 110, 116–17, 140nn87 and 94; signals of support (pins, etc.), 116, 137n57; and social norms, 116; and social status, 137–38nn61 and 62; and time preferences for donating, 132; and visibility, 115 gambling, 172–74, 656–57, 663, 687–88, 696 Gamson’s law, 370–71 GARP. See generalized axiom of revealed preference gender, 481–553; and aging, 455; and altruism, 483, 487, 512–25, 549n25; and blood donation, 281n86, 520; and challenging tasks, 483, 507–10; and charitable giving, 519–20; and competition, 483, 485–507, 548nn12–14; and cooperation, 512–25; and education choices, 504–7, 510; and exams, 482, 543–45; and gift exchange games, 264–65; and group identity, 254; and other-regarding preferences, 446, 487; and risk preferences, 482–83, 486, 498, 525–46, 551nn45 and 46; and “speaking up,” 483, 507, 510–12; and tipping in restaurants, 519–20; and voting behavior, 520, 548n4; and winner’s curse, 595; and the workplace, 523, 542 generalized axiom of revealed preference (GARP), 96, 176, 235–36, 278nn32, 34, and 35, 439–40, 442–43, 447–50, 469, 473n18 genes, 154, 173, 200, 201n7 gift exchange, 259–75; critical papers listed, 275–76; directions for future research, 274; and efficiency wage theory, 47–50, 260; field studies, 267–74; and fundraising, 132; gifts in kind vs. monetary gifts, 271–73; and incomplete contracts, 261–62; and monetary exchange models, 41–42; and other-regarding preferences, 218 gift exchange game, 48–49, 259–61, 264–67, 436 global game approach, 80n27 group identity, 253–55, 445 habits, 11–12, 78 hand washing, 692–93 hedonic states, 154, 184, 186 hoarding, 38 hormones, and competition, 492 incentives, and efficiency wage theory, 47–50 income, 5–9, 77, 97, 439. See also wages

•

741

inequality aversion, 183–84, 224, 230–31, 278n28; and gender, 518–19, 524; and learning, 687–88; and neurobiology, 183–85; social welfare preferences vs. difference aversion, 231–32. See also dictator game; ultimatum game inflation, 35, 37–38, 42–43, 57, 64–73, 71. See also macroeconomic policies information: auctions with insider information, 587–88; and bounded rationality, 16; and committee bargaining, 359–66; and consumption/savings decisions, 7; and elections, 381–84, 386–87, 422n68; and global game approach to resolving coordination problems, 30–32; information aggregation in committees, 400–410; information on contributions of others in public goods experiments, 105–6; and leadership giving, 113–14; and monetary exchange models, 41; and motives for charitable giving, 98; and price-setting game, 72–73; and rational expectations, 15–16; and sequential giving, 110, 112–14; and social interaction and learning in games, 678–82, 686–87; and swing voter’s curse, 406–10; and voter turnout, 397–98. See also political economy experiments institutionalized subjects. See token economies insula, 104, 163, 172, 177, 186, 187, 191, 196, 197, 199 insurance, 24–26 intentionality, 217, 220–22, 225, 228, 233–35, 277n18 interest rates, 38–39, 67–73 international trade and finance, 50–55, 57–59 interpersonal conflicts, 698–99 intertemporal choice and self-regulation, 178–83 intertemporal optimization problems, 2, 4–20. See also coordination problems investment, 19–20, 80nn25 and 28, 129 investment game, 240–42, 523–24, 537. See also trust game Iowa gambling task, 656–57, 663 jar-of-coins demonstration of winner’s curse, 292–95 jury trials, 352, 400–406, 422nn107 and 108 kidney exchange programs, 335n9 kindness, 222, 233–35. See also dictator game; fairness; other-regarding preferences; punishment; reciprocity; ultimatum game labor economics, 46–60, 78; and animal subjects, 440–41; and delegation/diffusion of responsibility in laying off workers, 249; early exploding offers, 323–26; efficiency wage theory and labor-market contracts, 47–50; enforcement of safety rules, 689–91; field analysis of workers’ reactions to unemployment

742

•

Subject Index labor economics (continued) spells, 46; field studies of wages and effort, 267–74; and gender, 523, 542; and gift exchange, 47–50, 259–74; and gifts in kind vs. monetary gifts, 271–73; and incomplete contracts, 261–62; job search models, 46, 50; labor-leisure trade-off, 47–50, 451; labor market clearinghouses (doctors), 318–26; labor search models, 46; labor supply, 47; market for PhD students, 323–28; and monetary policy, 73; and multisectoral macroeconomic experiments, 59–60; and personality/cognitive ability, 264–65; and risk preferences, 542–46; signaling in decentralized labor markets, 328–29, 338n45; and tax policies and unemployment benefits, 74–75; and token economies, 451; and wage rigidity, 262–63. See also unemployment; wages Lagos-Wright model of monetary exchange, 43 leadership: and charitable giving, 113–14, 116–17, 131, 137–38nn62, 65 and 66, 140n94; and coordination problems, 136n43; endogenous leadership, 117–18, 138n66; and monetary policy decisions, 68–69 learning, 638–702; and animal subjects, 443–44, 642, 646, 648–49, 668–71, 674–75; and auctions, 313; big eyes effect, 644–45; and certainty/reversed certainty effect, 648–49; and chasing previous results, 644–45; choice rules, 641–42; classical conditioning, 675–76; and cobweb model, 16–19; and cognitive strategies, 640–41, 671, 673–74, 687; constant-gain learning, 81n45; and consumption/savings decisions, 7–9, 11–12; and correlation effect, 645–46; decisions from description vs. decisions from experience (see decisions from experience); disjuncture between subjects’ beliefs and actions, 81n30; and dopamine neurons, 163; and dynamic environments, 668–72; and economics of small decisions, 638–702; effect of delay and melioration, 671–72, 702n11; emphasis-change training, 695; and exploration policy, 640–41, 657, 664, 674; and fictitious play, 659–60; “fictive learning,” 193–94; and framing, 685, 701; and gentle continual punishment, 690–91; hot stove effect, 663–65, 667, 696–97; individual differences, 656–57, 659; and inequality aversion, 687–88; inertia and surprise-triggers-change, 655–56, 658–59, 699; intergenerational learning, 12; and Iowa gambling task, 656–57, 663; I-SAW model, 657–61, 665–66, 699, 701n9; law of effect, 642–43; learned helplessness, 674–75; and limited feedback, 663–67; and loss aversion, 644–45, 661–62; and multiple alternatives, 672–75; naive sample model and probability matching, 660–61; negative effects of punishment, 688–89; neighborhood effect, 672–74; and neural basis of strategic thinking,

189, 192–94; and number of interacting agents, 678–80, 685; observational learning, 676–77; other-regarding preferences and adaptive learning, 218, 236–40; partial reinforcement extinction effect, 668–69; payoff variability effect, 642–47, 701n5; peer-to-peer learning, 12; probability learning, matching, and overmatching, 646–47, 670; properties of decisions from experience, 641–68; reinforcement learning, 193, 194, 640, 659–61, 668–69; and risk preferences, 175, 644–45, 661; shaping (successive approximation), 672–73; social interaction and learning in games, 677–88; spontaneous alternation, gambler fallacy, and response to patterns, 670; strategic teaching and influence value, 194–96; and swing voter’s curse, 408–9; transfer of learning to other tasks, 671; and ultimatum game, 219, 236–40, 676, 687–88; underweighting/overweighting of rare events, 647–51, 661–62, 670, 699, 700; very recent and wavy recent effects, 651–55, 658 learning-to-forecast experimental design, 15–18, 37, 70, 74, 78 learning-to-optimize experimental design, 15, 78 legislatures, 370, 372–74, 378–81. See also committee bargaining lesion studies, 154, 174, 177, 187, 200, 656–57 loser’s regret, 568–69, 624n10 loss aversion, 172–74, 177, 459, 468–69, 644–45, 661–62 lotteries, 92, 108–9, 119–25, 139nn75–78 and 83, 140n96; and animal subjects, 441; compared to auctions, 123–25, 139n83; compared to taxes, 139n75; compared to voluntary contribution mechanism, 120–21, 124–25; and dictator game, 244–45, 247; field studies, 122; fixed prize, 119–20, 123; multiple prizes, 122–23; revenue-dependent, 122; and risk preferences (see risk preferences); state-run lotteries, 139n75 macroeconomic policies, 61–78; and central banks, 65–73; and commitment vs. discretionary policies, 64–67, 81n45; directions for future research, 77–78; fiscal and tax policies, 73–78; and fiscal stimulus/Ricardian equivalence, 61–63; and group vs. individual policymaking, 67–69, 81n46; and labor economics, 73; monetary policies, 17–18, 61–73; pricing frictions and price-setting game, 72–73; and Taylor rule, 69–70 majority rule. See committee bargaining; elections and candidate competition; voting market design experiments, 290–339; airport takeoff and landing slot allocation, 295–300, 335nn10 and11, 336n15; and auctions with synergies, 605–7; college course allocation system, 329–33; eBay auctions, 307–16,

Subject Index 337nn27–30, 338nn33–37; labor market clearinghouses (doctors), 318–26; Medicare procurement auctions, 316–18; online dating, 328–29; and policymaking, 301–2; and professionals, 464; radio spectrum auctions, 294, 300–307, 335n9, 336n18, 337nn23–25; signaling in decentralized labor markets, 218, 328–29, 338n45; and winner’s curse, 292–95 market entry game, 667–68, 678, 680 markets: market for voluntary contributions (see charitable giving; fundraising); markets for votes, 415–18; monetary exchange models, 33–45; and multisectoral macroeconomics, 55–60; sunspot variables as coordination devices, 28–30; and supply of money, 36. See also international trade and finance matched contributions fundraising technique, 92, 108, 126–31, 140nn94 and 100 matching games, 189, 191, 194 Medicare procurement auctions, 316–18 memory, 9, 171, 189, 191, 192, 195, 198, 199, 667, 668 monetary economics, 33–45, 61–73. See also exchange-rate determination; inflation; international trade and finance; macroeconomic policies; prices money illusion, 43–45, 81n36 money supply, 36, 37, 43, 72–73. See also exchange-rate determination money-time choice (money-now vs. money-later) experiments, 13–14, 178–79, 442 motivation: and charitable giving, 91, 95, 97–110, 114, 127–28, 134nn16, 18, 22 and 25, 135nn23 and 28, 140nn94 and 96; crowding out intrinsic motivation, 97, 100–103, 126–28, 134nn24 and 25, 135n26, 140nn94 and 96, 281n86; and gifts in kind vs. monetary gifts, 271–73, 282n98; incentives and efficiency wage theory, 47–50; pat-on-the-back paradox, 695–96. See also gift exchange; labor economics; reciprocity multilateral bargaining experiments, 242–44 multisectoral macroeconomic, 55–60 mutual fate games, 678–80 neuroeconomics, 153–202; animal models, 154, 160, 162, 166, 173, 180, 189, 190, 194; brain stimulation experiments, 154, 175, 180, 181, 183, 188; charitable giving studies, 103–4, 135n28; described, 153–55; executive function/willpower studies (intertemporal choice and self-regulation), 178–83; eye-tracking studies, 190, 199–200; motivations for research, 154–55, 200; neural anomalies (brain lesions, autism, etc.), 154, 174, 176, 177, 187, 190, 196, 200, 656–57; neuroimaging (see neuroimaging); neuropharmacological exposure, 188; overview of neurobiology,

•

743

156–64; risk studies, 172–77; single neuron studies, 154, 158, 160–62; social preferences studies, 183–89; strategic behavior studies, 189–200 neuroimaging, 153–54, 164–77; experimental design considerations, 166–68; functional MRI (fMRI), 153, 164–77, 183–85, 188, 191, 194, 196, 199–200, 201nn7 and 8; image analysis, 168–72; positron emission tomography (PET), 164, 175, 177, 184; single positron emission computed tomography (SPECT), 164 neurotransmitters, 157–61, 164–65, 173, 188, 201n1 NP-complete problems, 298, 335n9 oil industry, 293, 582, 597 Okun’s law, 57, 81n42 online dating, 328–29 optimization problems. See coordination problems; intertemporal optimization problems orbitofrontal cortex (OFC), 175, 176, 184, 193, 656–57 other-regarding preferences, 183, 217–82; and adaptive learning, 218, 236–40; and age of subjects, 279n42; alternating-offer bargaining games, 222; and belief, 234–35; Bolton–Ockenfels model (2000), 217, 219, 222–25, 229, 231, 265, 275, 280n63; and charitable giving, 116; Charness–Rabin model (2002), 218, 230, 233–35, 276, 278n28; and children, 445–47; critical papers listed, 275–76; and delegation/diffusion of responsibility, 249–53; and demand-induced effects, 245–47, 280n60; and dictator game, 218–20, 235–36, 244–47; directions for future research, 230, 258, 274; and efficiency, 217, 235–36; and efficiency vs. equity trade-off, 217, 231–32; Fehr–Schmidt model (1999), 217, 222–25, 229, 231, 275; field studies, 255, 258, 267–74; and gender, 446, 487; generalizability of results to natural behavior, 255–59; and gift-exchange experiments, 218, 259–74; and group identity and social preferences, 253–55; heterogeneity among subjects’ preferences, 232, 235–36; and intentionality, 217, 220–21, 225, 228–29, 233–35, 277n18; and interpersonal conflicts, 698–99; and menu dependence, 276; methodological considerations/framing effects, 230–31; models/tests of models, 218–40 (see also specific models under this heading); and multilateral bargaining experiments, 242–44; and perception of actions by self and others, 249, 275; and personality, 257–58, 264–65; price sensitivity of, 235–36; and principle-agent games, 249–53, 261–62; and procedural fairness, 247–49; and professionals, 463–64; Rabin model (1993), 219, 222, 277n9; and rational choice theory, 235–36; and reciprocity,

744

•

Subject Index other-regarding preferences (continued) 233–35, 278nn28 and 29; and representative sample, 460; social welfare preferences vs. difference aversion, 231–32; third-party rejection payoff games, 228–29; and three-player sequential step-level public goods game, 238–39; and trust (investment) game, 240–42; and ultimatum game, 218–19 overlapping generations models, 2, 21, 34, 36–38, 61–63, 75–78 oxytocin, 188 peasant-dictator game, 64–65 pension game, 76–77 personality: Big Five characteristics, 264–65, 281n83; borderline personality disorder, 196; and competition, 494; and consumption/savings decisions, 9; genetic components, 173, 201n7; and gift exchange game, 264–65; and other-regarding preferences, 257–58, 264–65; and strategic thinking, 191; and trust game, 257–58 Phillips curve, 57, 64–67, 70, 73 political economy experiments, 347–424; committee bargaining, 350–81, 420nn24–26; directions for future research, 410, 418–19; effects of voting rules and procedures on information aggregation in committees, 352; elections and candidate competition, 351–52, 381–91; information aggregation in committees, 352, 400–406; jury trials, 352, 400–406, 422nn107 and 108; methodological considerations, 348–50; and positive political theory, 349; and social choice theory, 349–51, 400, 410; swing voter’s curse, 406–10; voter turnout, 392–400; voting methods reflecting preference intensity, 352, 410–18 positron emission tomography (PET), 164, 175, 177, 184 poverty traps, 21–24, 27 precuneus, 191, 196, 197, 199 prefrontal cortex, 164, 180–83, 186–88, 191–92, 195–200, 198 prices: and consumption/savings decisions, 7; and currency markets, 51–55; and money as a unit of account, 33–38, 43–45; and multisectoral macroeconomic experiments, 56–57, 59; price forecasting, 15–20; price of charitable giving, 126–31, 483 (see also under altruism); price stickiness, 17–18, 45, 70, 78, 81n47. See also market design experiments price-setting games, 43–45, 72–73 principle-agent experiments, 249–53, 261–62, 462, 464 prisoner’s dilemma game, 42, 48, 137n58, 138n67, 184, 277n9; defection in, 234; and gender, 513, 520–21; and group identity, 255; and personality, 264; and social interaction and

learning in games, 683–86, 701. See also social dilemma game product updating, 697 professionals, as subject population, 436–37, 461–68, 470–71, 611, 625–26n31 prospect theory, 172–74, 647, 650, 661 psychological game theory, 234, 235, 253, 275, 276, 276n3 public goods, and legislative bargaining, 372–74, 378–81 public goods, contributions to. See charitable giving; fundraising; voluntary contribution mechanism public goods game: five-player linear public goods game, 243; and gender, 483, 513, 520–24; linear public good game (see voluntary contribution mechanism); and social interaction and learning in games, 683, 685; three-player sequential step-level public goods game, 238–39 punishment: costs of punishment, 229; and delegation/diffusion of responsibility, 252; gentle continual punishment, 690–91; and methodological considerations in experiments, 231; negative effects of, 688–89; and neurobiology, 155, 184, 186, 188; and personality, 264; punishing unfair/unkind behavior, 184, 220–21, 229. See also ultimatum game quality-of-life policing strategy, 692 Race to 100, 466 radio spectrum auctions, 294–95, 300–307, 335n9, 336n18, 337n23, 588–90, 598, 605 raffles. See lotteries rational choice theory, 176–77, 235–36, 392, 424n131, 438, 448–49, 639 rational expectations, 14–20, 36, 37, 71, 73, 236, 384. See also coordination problems rebates, 92, 126–31 reciprocity, 183, 281nn92–94; directions for future research, 274; field studies of wages and effort, 267–74, 281nn92–94; and fundraising, 109, 110, 114; and group identity, 255; and hidden costs of control, 261; and investment (trust) game, 241; and methodological considerations/framing effects, 231; and models of other-regarding preferences, 222, 234, 278n29; negative vs. positive reciprocity, 155, 269, 281n96; and neurobiology, 183; and other-regarding preferences, 233–35; psychological game-theoretic models, 234; and Rabin’s model of other-regarding behavior, 222; and social interaction and learning in games, 683–87; and social norms, 234; and strategic thinking, 196. See also gift exchange religious institutions, 92, 114–15, 254

Subject Index representative-agent assumption, 1–2, 4, 7, 9–11, 79n5 representative sample, 435–37, 455–61, 470–71 revealed preferences, 154, 183. See also generalized axiom of revealed preference rewards, 164, 172–86, 189, 196. See also delayed gratification; motivation; risk preferences Ricardian equivalence, 51, 61–63 risk preferences, 8, 14, 123, 442, 524; and age of subjects, 542; and animal subjects, 441–43; and auctions, 565, 567–68, 624nn3 and 4, 625n12; and causal influences (induced stress, etc.), 175–76; and children, 529, 542; and cognitive ability, 264; and committee bargaining, 369, 376; and competition, 486–87, 490–91, 498; and consumption/savings decisions, 5, 6, 8; and discount rates in intertemporal choice experiments, 178–81; and the elderly, 452–53; and elicitation methods, 483, 525, 530–33, 541; and exams, 482, 543–45; and gender, 482, 483, 486, 498, 525–46, 551nn45 and 46; and global game approach to resolving coordination problems, 32; and height, 542; and labor economics, 542; and learning, 175, 644–45, 661; and money-time choices, 14; neuroimaging studies, 172–77; and professionals, 467–68; and prospect theory, 172–74 (see also prospect theory); and representative sample, 458–60; stability of, 538–42; statistical moments of reward distributions, 172; and subject populations, 469; and voter turnout, 397 Rotten Kid Theorem (Becker), 445 safety devices and buying-using gap, 693–94 safety rules, enforcement of, 689–91 SAT scores, 543–45, 594–95 savings decisions. See consumption and savings decisions self-interest, 217–18; and children, 446; and competitive markets, 217, 227; deviations from self-interested behavior, 183–89, 217, 221–22, 231 (see also dictator game; other-regarding preferences; ultimatum game); “standard” economic model, 217, 218, 227; and voting behavior, 377. See also dictator game; prisoner’s dilemma game; social preferences; ultimatum game serotonin, 173, 175, 188 Shapley-Shubik market game, 3 signaling: and auctions, 293, 409, 583, 592, 626nn38 and 41 (see also auctions); and cellular structure of the brain, 156–60; cognitive demand of, 114; in decentralized labor markets, 328–29; and dictator game, 246; and gender/“speaking up,” 511; and global game approach to resolving coordination problems, 31–32; and jury trials, 401–6; and lead donor, 116–17; and motives for charitable giving, 95,

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745

106–7, 115, 135nn30 and 34; policy implications for public announcements, 32; and professionals (lobbying game), 464; signaling generosity, 106–7, 115; signaling quality of charities, 110–17; signaling wealth/ability, 135nn30 and 34; signals of support (pins, etc.), 116, 137n57; and sunspot variables as coordination devices, 30 silent auctions, 123 small-decision problems, 638–702. See also clicking paradigm; decisions from experience; learning social choice theory, 349–52, 400, 410 social contract, 77 social dilemma game, 138n69, 184, 521. See also prisoner’s dilemma game social distance, and charitable giving, 105, 106, 108 social groups, evolution of, 696–97 social interaction and learning in games, 677–88 social networks, 258 social norms, 7–8, 42, 106–7, 116, 196, 225, 234, 265 social planner, 9–11, 22, 80n10, 92 social preferences: and group identity, 253–55; neurocircuitry of, 183–89; social welfare preferences vs. difference aversion, 231–32. See also altruism; dictator game; fairness; inequality aversion; punishment; reciprocity; ultimatum game social security systems, 75–76 social status, 117, 137–38nn61 and 62 “speaking up,” and gender, 483 stag hunt game, 192, 698–99 strategic thinking studies: and beliefs about others, 190–92; and the elderly, 452, 454; and gender, 522–23, 549n24; and learning, 192–94; neural basis of strategic thinking, 189–200; and sophistication, 194, 198, 201n14, 590, 678; strategic awareness, 189–90; strategic teaching and influence value, 194–96. See also cognition striatum, 163, 172, 175, 177, 184, 185, 186, 191, 193 subject populations, 435–75; animal subjects, 437, 438–44, 469 (see also animal subjects); and auctions, 570–71, 592–93, 611, 625–26n31; children, 437, 444–49, 469–71 (see also children); and consumption/savings decision experiments, 7–8; and definition of macroeconomic experiments, 3; and dictator game, 446–47, 456–57; the elderly, 75–77, 437, 451–56, 461, 469, 542; and generalizability of other-regarding preferences results to natural behavior, 255–59; and gift exchange game, 266, 436; and group identity experiments, 255; and multisectoral macroeconomic experiments, 56–57; professionals (subjects with relevant task experience), 436–37, 461–68, 470–71, 611, 625–26n31; representative sample, 435–37, 455–61, 470–71; and robustness of experimental

746

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Subject Index subject populations (continued) results, 435; and social norms, 7–8; subjects in token economies, 437, 449–50, 469; and trust game, 256–57, 445–46, 455–56, 471; and ultimatum game, 218, 232, 446–47, 456–57, 470; and voluntary contribution mechanism (VCM; linear public good game), 256, 444–45, 470—71; volunteer artifact, 472n2, 473n25. See also gender sunspot variables as coordination devices, 27–30, 80n25 superior temporal sulcus (STS), 195 swing voter’s curse, 406–10 takeover game, 590–92 taxes, 42–43, 61–63, 73–78, 97, 100–103, 134nn24 and 25, 139n75 telencephalon, 162–64 tempero-parietal junction (TPJ), 164, 192, 200 temptation goods, 135n38, 179, 183 terrorism, 694–95 testosterone, 188 “theory of mind,” 189, 190, 192, 195 third-party rejection payoff games, 228–29 time preferences, 442, 470. See also discounting; headings beginning with intertemporal tipping in restaurants, 519–20 token economies, 437, 449–50, 469. See also charitable giving; fundraising transcranial direct current stimulation (tDCS), 175, 183 transcranial magnetic stimulation (TMS), 180, 181, 183, 188 trust, 118, 188 trust game, 48, 549–50n30; and children, 445–46; and communication, 234–35; compared to gift exchange game, 260; critical papers listed, 276; directions for future research, 258; and gender, 513–14; and group identity, 255; investment game and other-regarding preferences, 240–42; methodological considerations/framing effects, 231; and personality, 257–58; and professionals, 464; and representative sample, 455–56, 461; and strategic thinking, 196; and subject populations, 256–58, 445–46, 455–56, 471 two-armed bandit problems, 664–65 ultimatum game, 218–19, 227–28, 279n42, 689; and children, 446–47; compared to dictator game, 219–20; compared to market games, 227–28; critical papers listed, 275–76; described, 218, 277n4, 549n29; directions for future research, 230; efficiency vs. equity trade-off, 219–20, 231–32, 276 (see also inequality aversion); frequency of disadvantageous counteroffers, 222; and gender, 513–14; and intentionality, 220–22, 225, 228; and learning, 219, 236–40, 676, 687–88; methodological considerations/framing effects, 230–31, 233;

and models of other-regarding preferences, 219, 222–40; and neurobiology, 187–88; one-shot vs. repeated trials, 230–31; and punishing unfair behavior, 220–21, 228; and reciprocity, 222; and representative sample, 456–57, 460; and reward neurocircuitry, 184, 187–88; robustness issues, 218; and social norms, 196; and stake size, 218; and subject populations, 218, 232, 446–47, 456–57, 470; three-person games, 225–28, 456–57; utility function, 218, 221–24, 233; and verbal punishment, 229 unanimity rule. See jury trials unemployment, 6, 46, 50, 57, 64–75, 81n42, 262–63, 697–98. See also labor economics Unlikely Virtues Scale, 257 utility function: and alternating-offer bargaining games, 222; and dictator game, 218, 224–25; other-regarding behavior and utility maximization, 235–36; and reciprocity, 222; and ultimatum game, 218, 221–24, 233 visibility, and charitable giving, 105–6, 108, 115, 135n34 voluntary contribution mechanism (VCM; linear public good game), 94–95, 138n71, 279n41; and children, 444–45; compared to auctions, 124–25; compared to lotteries, 120–21, 124–25; and dynamic giving, 118–19; and the elderly, 453; and endogenous leadership, 117–18; and gender, 521–22; and intentionality vs. decision errors, 133n8; and other-regarding preferences, 116; and personality, 264; and professionals, 464; and representative sample, 459–60; and response time, 136n38; and sequential giving, 112–13, 116; and subject populations, 256, 444–45, 470–71; and visibility, 105–6 voluntary giving. See charitable giving voting, 349–52, 361–419; and backward induction, 362, 365, 366; directions for future research, 410; and economic growth, 22–24; effects of voting rules and procedures on information aggregation in committees, 352; expressive voting, 398–99; and gender, 520, 548n4; logrolling/vote trading, 352, 414–15; markets for votes, 415–18; qualitative voting, 352, 413–14; and rational expectations, 384; and redistributive social contract, 77; retrospective voting, 384–87; sophisticated voting, 361–66; storable votes, 352, 411–13; swing voter’s curse, 406–10; tyranny of the majority, 411, 412; vote balancing, 407; voter turnout, 352, 392–400; voting methods reflecting preference intensity, 352, 410–18. See also committee bargaining; elections and candidate competition; jury trials wages: efficiency wage theory, 47–50, 260; field studies of wages and effort, 267–74,

Subject Index 281nn92–94; and job search models, 46; and multisectoral macroeconomic experiments, 59–60; and tax policies and unemployment benefits, 74–75; wage offers and workers’ effort, 48–50, 259–74, 280n76, 281nn88–96; wage rigidity, 262–63 wallet game, 588–89 warm-glow altruism, 97–104, 134nn18, 22 and 25, 183

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747

warnings, timing of, 693 welfare, 21–24, 74–78 willpower, 178–83 winner’s curse, 292–95, 408–9, 468, 564, 582–83, 590–98, 619 workers. See labor economics working memory, 9, 191, 192, 195, 198 zero-sum games, 133n8, 465