Essays on Bounded Rationality in Applied Game Theory

Dissertation

Presented in Partial Fulﬁllment of the Requirements for the Degree Doctor of Philosophy in the Graduate School of The Ohio State University

Matthew Thomas Jones, B.S., M.A.

Graduate Program in Economics

The Ohio State University

2012

Dissertation Committee:

James Peck, Co-Advisor (Chair) Dan Levin, Co-Advisor John Kagel c Copyright by

Matthew Thomas Jones

2012 Abstract

Departures from fully rational behavior due to cognitive limitations or psychological phe- nomena are typically referred to by economists as boundedly rational behavior. In this dissertation, I study how bounded rationality impacts cooperation in repeated games, herding behavior and bidding in online auctions. The methods I use include theoretical modeling and empirical analysis of data collected in controlled laboratory experiments as well as data from the ﬁeld. This research contributes to the understanding of the consequences of bounded rationality in strategic interactions.

In the first chapter, I investigate whether cooperation in an indefinitely repeated prisoner’s dilemma is sensitive to the complexity of cooperative strategies. I use an experimental design which allows manipulations of the complexity of these strategies by making either the cooperate action or the defect action state-dependent. Subjects are found to be less likely to use a cooperative strategy and more likely to use a simpler selfish strategy when the complexity of cooperative strategies is increased. The robustness of this effect is supported by the

ﬁnding that cooperation falls even when the defect action is made state-dependent, which increases the complexity of punishment-enforced cooperative strategies. A link between subjects’ ACT scores and the likelihood of cooperating is found, indicating that greater cognitive ability makes subjects more likely to use complex strategies. Behavior when subjects play multiple simultaneous games is compared to their behavior in isolated single games,

ii providing evidence that the additional cognitive cost of playing multiple games also limits cooperation within this environment.

Despite numerous applications, the importance of capacity constraints has so far received little attention in the literature on herding behavior. I attempt to address this issue in my second chapter by constructing a simple model of herding with capacity constraints and studying behavior in this environment experimentally. The model predicts and experimental results confirm that capacity constraints can attenuate herding, with the size of the effect dependent on the penalty of choosing an option after its capacity has been reached. For subjects earlier in a sequence of choices, behavior without a capacity constraint does not differ markedly from that observed in comparable experiments despite the fact that preceding choices are made by computers with fixed, commonly known choice rules rather than other humans. For subjects later in a sequence of choices, I find evidence that whether they respond rationally to the capacity constraint is dependent on factors such as the depth-of-reasoning involved in the fully rational equilibrium and the subject’s cognitive ability.

The third chapter of this dissertation is a study of data on bidding behavior in eBay auctions of Amazon.com gift certiﬁcates. I ﬁnd that 41.1% of winning prices in these auctions exceed the face value, which is an observable upper bound for rational bidding because

Amazon.com sells certiﬁcates at face value. Alternative interpretations are explored, but bidding fever seems to be the most plausible explanation for the observed behavior.

iii Acknowledgments

I would like to thank Dan Levin and James Peck for their invaluable guidance and support. I am also very grateful to John Kagel for his advice and feedback. This work also beneﬁtted from the comments and assistance of Michelle Chapman, Caleb Cox, P.J. Healy,

Asen Ivanov, Mark R. Johnson, Gary Kennedy, Matthew Lewis, Brandon Restrepo, Michael

Sinkey, John Wooders, Lixin Ye, participants of the microeconomics brownbag seminar and the theory/experimental reading group at Ohio State, and seminar participants at the 2011

ESA International Meeting, the 2011 PEA Conference, Kent State University, the Univer- sity of Memphis and the Federal Trade Commission. This work is supported by the NSF under Grant No. SES-1121085. Any opinions, ﬁndings and conclusions or recommendations expressed are those of the author and do not necessarily reﬂect the views of the NSF.

iv Vita

October 13, 1984 ...... Born - Pittsburgh, Pennsylvania

May 2007 ...... B.S. in Economics and Mathematics - Saint Vincent College August 2008 ...... M.A. in Economics - The Ohio State University 2007-present ...... Graduate Teaching/Research Asso- ciate - The Ohio State University

Publications

Research Publications

Jones, M.T. (2011). Bidding fever in eBay auctions of Amazon.com gift certiﬁcates. Eco- nomics Letters 113(1), 5-7.

Fields of Study

Major Field: Economics

v Table of Contents

Page

Abstract ...... ii

Acknowledgments ...... iv

Vita...... v

List of Tables ...... viii

List of Figures ...... x

1. Strategic Complexity and Cooperation: An Experimental Study ...... 1

1.1 Introduction ...... 1 1.2 Theoretical Background ...... 6 1.3 Experimental Design ...... 9 1.4 Research Questions ...... 12 1.5 Results ...... 15 1.5.1 Aggregate Cooperation ...... 16 1.5.2 Strategy Inference ...... 23 1.5.3 Regression Analysis ...... 29 1.6 Conclusion ...... 37

2. An Experiment on Herding with Capacity Constraints ...... 39

2.1 Introduction ...... 39 2.2 Related Literature ...... 42 2.3 Model ...... 46 2.3.1 Risk-Neutral Bayesian Nash Equilibrium ...... 48 2.3.2 Bounded Rationality ...... 50 2.4 Experimental Design ...... 53

vi 2.5 Experimental Questions and Results ...... 56 2.5.1 Eﬀects of the Capacity Constraint ...... 62 2.5.2 Subjects Satisfying Basic Rationality ...... 66 2.5.3 Rationality vs. Bounded Rationality ...... 72 2.6 Conclusion ...... 80

3. eBay Auctions of Amazon.com Gift Certiﬁcates: A Study of Bidding Fever in the Field ...... 82

3.1 Introduction ...... 82 3.2 Data ...... 83 3.3 Interpretation ...... 84 3.4 Alternative Interpretations ...... 87 3.5 Regression Analysis ...... 88 3.6 Conclusion ...... 90

Appendices 92

A. Appendix to Strategic Complexity and Cooperation: An Experimental Study . . 92

A.1 Directed Graph Representations of Selected Automaton Strategies in Each Treatment ...... 92 A.2 Instructions and Screenshots ...... 94 A.2.1 Phase I Instructions ...... 94 A.2.2 Phase II Instructions ...... 97

B. Appendix to An Experiment on Herding with Capacity Constraints ...... 105

B.1 Derivation of RNBNE ...... 105 B.2 Derivation of Level-k Strategies ...... 107 B.3 Risk Aversion ...... 109 B.4 Instructions and Screenshots ...... 110

Bibliography ...... 119

vii List of Tables

Table Page

1.1 Treatments ...... 11

1.2 Repeated Game Lengths ...... 12

1.3 Frequency of Cooperation ...... 18

1.4 Summary of Stage Outcomes ...... 19

1.5 Candidate Automaton Strategies ...... 24

1.6 Maximum Likelihood Estimates of Strategy Prevalence ...... 25

1.7 Probits Reporting Marginal Eﬀects of Treatments and History of Play . . . . 30

1.8 ACT and SAT-ACT Concordance Score Summary Statistics ...... 32

1.9 Probits Reporting Marginal Eﬀects of ACT Percentile, Separated by Treatment 33

1.10 Probits Reporting Marginal Eﬀects of ACT Percentile, Treatment Interactions 36

2.1 Summary of Strategies by Treatment and Setting ...... 60

2.2 Predicted vs. Actual Eﬀects of Treatment and Setting on Strategies . . . . . 63

2.3 Mean Strategies, First Round and Last Round in Each Setting ...... 65

2.4 Eﬀects of Treatment/Setting on Strategies of Subjects Satisfying Basic Ratio- nality ...... 68

2.5 Cost Level in Trial Rounds and Rounds 1-6 of MIXED/ORDERED . . . . . 69

viii 2.6 ACT and SAT-ACT Concordance Score Summary Statistics ...... 71

2.7 Probits Reporting Marginal Eﬀects of ACT/Major on Satisfying Basic Ratio- nality ...... 72

2.8 Transition Matrix Showing Player 3 Best-Fitting Theory Across Settings . . 77

2.9 Transition Matrix Showing Player 4 Best-Fitting Theory Across Settings . . 77

2.10 Relationship Between Test Scores/Major and MSD Scores - OLS Regressions 79

3.1 Descriptive Statistics ...... 83

3.2 Summary of Overbidding ...... 84

3.3 Overbidding by Time and Day of Week ...... 85

3.4 Overbidding and Winning Bidder’s Rating ...... 86

3.5 OLS Regression - Dependent Variable: Percentage Overbid ...... 89

ix List of Figures

Figure Page

1.1 Payoﬀ Tables ...... 10

1.2 Cooperation by Round ...... 17

1.3 Cooperation by Round: NOSWITCH/NOSWITCH-R ...... 22

2.1 RNBNE Strategies for Players 3 and 4 ...... 49

2.2 Level-k Strategies of Player 3 ...... 51

2.3 Level-k Strategies of Player 4 ...... 52

2.4 Computer Player Strategies ...... 54

2.5 Player 4 Strategies in NAIVE-MIXED ...... 55

2.6 Distribution of Strategies by Treatment/Setting/Preceding Player Choice . . 57

2.7 Distribution of Strategies by Treatment and Setting ...... 61

2.8 Distribution of BR Subjects’ Strategies by Treatment and Setting ...... 67

2.9 Strategies with No Capacity Constraint, Rounds 1-6 of MIXED/ORDERED 70

2.10 Player 3 Mean Squared Deviation from Equilibrium ...... 74

2.11 Player 4 Mean Squared Deviation from Equilibrium ...... 75

A.1 Always Defect (AD) ...... 92

x A.2 Always Cooperate (AC) ...... 93

A.3 Grim Trigger (GT) ...... 93

A.4 Tit-for-Tat (TFT) ...... 94

A.5 Screen 1 (Single Game Rounds) ...... 99

A.6 Screen 2 (Single Game Rounds) ...... 100

A.7 Screen 3 (Single Game Rounds) ...... 101

A.8 Screen 1 (Multiple Game Rounds) ...... 102

A.9 Screen 2 (Multiple Game Rounds) ...... 103

A.10 Screen 3 (Multiple Game Rounds) ...... 104

B.1 Player 3 Choice Screen ...... 115

B.2 Player 4 Choice Screen ...... 116

B.3 Player 3 Feedback Screen ...... 117

B.4 Player 4 Feedback Screen ...... 118

xi Chapter 1: Strategic Complexity and Cooperation: An Experimental Study

1.1 Introduction

To implement a strategy in a repeated game, a player must process and respond to information she receives from her environment such as the behavior of opponents, the state of nature, etc. Intuitively, one can say that the complexity of a repeated game strategy depends on the amount of information that must be processed to implement it. For example, consider a repeated oligopoly pricing game in which firms set a price in each stage after receiving information about demand conditions and the prices set by rivals. To use a competitive pricing strategy, a firm sets its price equal to a constant marginal cost in each stage. To use a collusive pricing strategy, a firm sets its price conditional on the demand state as well as the prices set by rival firms. Hence, the collusive pricing strategy can be called more complex because implementing it involves processing more information. If there are costs associated with this information processing in the form of management compensation, operating costs, etc., they can affect the firm’s pricing strategy choice and make a relatively complex collusive strategy less likely to be used. Similarly, cognitive costs associated with information processing may influence repeated game strategy choice on the individual level, yielding important consequences for cooperation and efficiency.

1 Theoretical literature suggests that strategic complexity is a practical equilibrium selection criterion in repeated games with both cooperative and selﬁsh equilibria. Rubinstein

(1986) and Abreu and Rubinstein (1988) show that incorporating strategic complexity costs into the preferences of players in the infinitely repeated prisoner’s dilemma causes the efficient cooperative equilibrium to unravel. Hence, in repeated games where efficiency depends on players adopting relatively complex cooperative strategies rather than simple selfish strategies, cognitive costs associated with implementing complex strategies may discourage cooperation and harm efficiency. Accounting for strategic complexity can also have important implications in the study of market games. Fershtman and Kalai (1993) show that collusion in a multi-market duopoly may be unsustainable when strategic complexity is bounded. Gale and Sabourian (2005) consider a market game with a finite number of sellers, which normally has both competitive and non-competitive equilibria, and show that only the competitive equilibria remain with strategic complexity costs. These results demonstrate that limitations on strategic complexity can have important consequences in abstract environments as well as applied settings, which highlights the need for relevant empirical evidence.

In this study, I investigate whether cooperation in an indefinitely repeated prisoner’s dilemma is sensitive to the complexity of cooperative strategies. I use an experimental design which allows manipulations of the implementation complexity of strategies by making either the cooperate or defect action state-dependent. I find that subjects are less likely to use a cooperative strategy and more likely to use a simpler selfish strategy when the complexity of cooperative strategies is increased. The robustness of this effect is supported by the finding that cooperation falls even when the defect action is made state-dependent, which increases the complexity of punishment-enforced cooperative strategies. These results provide evidence

2 that cognitive costs associated with strategic complexity can have an impact on cooperation and eﬃciency.

Cooperation in the indefinitely repeated prisoner’s dilemma has been the subject of many experimental studies.1 Roth and Murnighan (1978), Murnighan and Roth (1983) and Blon- ski et al. (2010) find that cooperation in this game depends on the payoffs and continuation probability, while Dal Bo and Frechette (2011a) find that subgame perfection and risk domi- nance are necessary but not sufficient conditions for cooperation. Dal Bo (2005), Camera and

Casari (2009), and Duffy and Ochs (2009) provide evidence that the indefinitely repeated prisoner’s dilemma fosters cooperation because it allows players to use punishment-enforced cooperative strategies. Though cooperation is commonly observed in these experiments, to my knowledge this is the first study to investigate whether cooperation in this game is affected by limitations on strategic complexity.

Some extant experimental evidence suggests that behavior in the prisoner’s dilemma is sensitive to cognitive costs and abilities. In a meta-study of prisoner’s dilemma experiments,

Jones (2008) identifies a positive relationship between cooperation and the average SAT score of the institution from which subjects are drawn. Cooperation in repeated prisoner’s dilemmas is found to fall when subjects are required to complete an unrelated memory task while playing (Milinski and Wedekind 1998, Duffy and Smith 2011) and when they must rely on memory to track the actions of multiple opponents in a random sequence (Winkler et al. 2008, Stevens et al. 2011). Bednar et al. (2012) find that cooperation in an indefinitely repeated prisoner’s dilemma is reduced when subjects incur the additional cognitive cost of playing another repeated game simultaneously. These studies indicate that cognitive costs

1There is a rich literature on cooperation in similar environments, such as indeﬁnitey repeated oligopoly games (Holt 1985, Feinberg and Husted 1993) and public goods games (Palfrey and Rosenthal 1994) as well as prisoner’s dilemmas with costly punishment (Dreber et al. 2008), imperfect monitoring (Aoyagi and Frechette 2009) and noisy implementation of intended actions (Fudenberg et al. 2012).

3 can have a negative impact on cooperation in the prisoner’s dilemma, but the mechanism through which this relationship operates has not yet been identiﬁed. I address this question by investigating whether cognitive costs related to the complexity of strategic implementation reduce cooperation in the spirit of the theoretical work pioneered by Rubinstein.

In this experiment, the complexity of strategic implementation is increased through random switching between permutations of a three-by-three version of the prisoner’s dilemma within each repeated game. Each treatment employs two payoﬀ tables with a strictly dominated dummy action added to the cooperate and defect actions, with the position of the dummy action varied between tables. Before each stage of a repeated game, one of the two payoﬀ tables is drawn randomly and publicly announced to apply in that stage. This feature of the design can be viewed as increasing complexity by requiring subjects to condition their action choices on observable changes in the state of nature in order to use certain types of strategies.

In one treatment, the positions of the cooperate and dummy actions are permuted between the two payoff tables. Because cooperating requires subjects to account for random switching between tables in order to choose the correct action, cooperative strategies are more complex in this treatment than in a baseline treatment in which the positions of the cooperate, defect and dummy actions are the same in both tables. Less aggregate cooperation is observed, and subjects have a greater tendency to adopt a simple selfish strategy in this treatment than in the baseline. This effect of greater complexity is found to be robust in another treatment which increases the complexity of cooperative strategies in a different way. In this treatment, the dummy action is permuted with the defect action instead of the cooperate action so that defecting requires subjects to account for random switching between payoff tables. Relative to the baseline, this treatment increases the implementation

4 complexity of selﬁsh strategies as well as punishment-enforced cooperative strategies such that these cooperative strategies remain the most complex. If there is an upper bound on the complexity of strategies subjects can use or the cognitive costs of complexity are convex, less cooperation is expected in this treatment. Indeed, aggregate measures and strategy inference reveal less cooperation in this treatment than in the baseline.

The idea that cognitive costs of strategic complexity affect cooperation is further supported by data on subjects’ ACT scores, which indicate a positive relationship between cognitive ability and cooperation. To my knowledge, this is the first study to find evidence of such a relationship at the individual level. This relationship is consistent with the idea that cognitive costs of strategic complexity affect strategy choice because cooperative strategies are generally more complex than playing selfishly, and subjects with greater cognitive ability should be more able to bear the cognitive cost associated with this complexity.

A second source of increased cognitive cost is introduced in this experiment to investigate possible interactions with the complexity treatments. Extant experimental evidence2 suggests that the cognitive cost of playing multiple games simultaneously aﬀects behavior in the individual games compared to when they are played in isolation. For half of each session of the experiment, I ask subjects to participate in multiple prisoner’s dilemma games simultaneously, and I ﬁnd that the multiple game environment reduces the use of relatively complex cooperative strategies. Cooperation does not fall between phases when the single games phase is played before the multiple games phase, but a negative impact on cooperation is found when multiple games phases are compared to parallel single games phases.

Consistent with previous literature,3 I also ﬁnd that subjects are less likely to mix between

2See Winkler et al. (2008), Cason and Gangadharan (2010), Cason et al. (2010), Guth et al. (2010), Savikhin and Sheremeta (2010), Bednar et al. (2012) and Stevens et al. (2011). 3See Cason and Gangadharan (2010), Cason et al. (2010), Savikhin and Sheremeta (2010) and Bednar et al. (2012).

5 diﬀerent types of strategies in simultaneous games in treatments where strategies are more complex to implement. Evidence that subjects learn to adopt cooperative strategies over the course of a session is found in all treatments, but it appears that this learning is hindered by the increased cognitive cost of playing multiple games.

1.2 Theoretical Background

The most popular theoretical approach to studying strategic complexity in repeated games is the theory of games played by finite state automata.4 This approach measures the implementation complexity of a repeated game strategy by the number of states in the minimal finite automaton which implements the strategy. I adopt this measure of strategic complexity in designing the experiment and analyzing the results. It can be thought of as a metaphor for measuring complexity by the fineness of the partition of the game history required to implement a strategy which conditions on that history. Another interpretation of this definition is due to Kalai and Stanford (1988), who show that the number of states in the minimal finite automaton implementing a strategy is equal to the number of different subgame strategies the original strategy induces. This concept of complexity does not capture the complexity associated with computing optimal actions and strategies, nor does it address the complexity associated with decisions under uncertainty because it is defined in a complete information environment. Instead, it measures the complexity of information processing or monitoring required to implement a strategy. Increasing the amount of information that must be processed means that the strategy-implementing automaton must contain more

4This approach was first suggested by Aumann (1981). See Chatterjee and Sabourian (2009) for a recent survey of repeated game applications of finite automata. See Johnson (2006a) and Salant (2011) for applications of finite automata in models of boundedly rational individual choice.

6 states to keep track of its environment and follow a given plan of how to react to incoming

information.

A repeated game strategy is modeled in terms of ﬁnite automata as follows. A strategy

consists of a ﬁnite number of machine states, Q, an initial state, q0 ∈ Q, a behavior function,

λ : Q → A, mapping from states into the set of possible actions, A, and a state transition function, µ : Q × S → Q, mapping from states and the opponent’s last observed action, s ∈ S, into states.5 The simple measure of strategic complexity provided by this model is the minimal number of states that can be contained in Q such that the automaton can implement the strategy.6 For example, consider a strategy of Tit-for-Tat played in a standard prisoner’s dilemma in which the set of possible actions is A = S = {C,D} where C is cooperate

and D is defect. The automaton implementing Tit-for-Tat in this game is represented by

the set of states, Q = {1, 2}, where 1 is the initial state, the behavior function deﬁned

by λ(1) = C, λ(2) = D, and the state transition function deﬁned by µ(1,C) = µ(2,C) =

1, µ(1,D) = µ(2,D) = 2. The automaton implementing Always Defect in this game is

represented by the set of states, Q = {1}, where 1 is the initial state, the behavior function,

λ(1) = D, and the state transition function, µ(1,D) = µ(1,C) = 1. Since Tit-for-Tat has

5This type of finite automaton, in which the transition function takes as its domain the cross-product of states and only the opponent’s observed action rather than the actions of both players, is known as a Moore machine. 6Others have attempted to refine the above finite automata model to provide a more robust measure of strategic complexity. Banks and Sundaram (1990) propose that the number of state transitions in an automaton should be considered as well as the number of states, which would reflect more precisely the amount of monitoring necessary in implementing a strategy. Johnson (2006b) defines the complexity of a strategy in terms of existing definitions of algebraic complexity. He studies the algebraic properties of the minimal automaton representation of a strategy and provides a ranking of strategic complexity by whether implementation requires an automaton which can detect sequences, count and/or repeat cycles. These complexity measures provide a more complete ranking of the strategies considered in this experiment, but they remain consistent with the ranking in terms of the number of states in the minimal strategy- implementing automaton. I use the number of states to measure complexity due to its simplicity and its relative popularity in the literature.

7 two states and Always Defect only one, Tit-for-Tat is considered to be a more complex strategy.

The finite automata definition of strategic complexity has been used by Rubinstein (1986) and Abreu and Rubinstein (1988) to show that the set of equilibria of the inifinitely repeated prisoner’s dilemma is drastically reduced when a minimal (lexicographic) cost of states in the strategy-implementing automaton is added to players’ preferences. An automaton implementing a cooperative equilibrium strategy is more complex than one implementing a strategy of Always Defect because more states are needed for an automaton to enforce cooperation by monitoring the opponent and punishing defection. The efficient cooperative equilibrium unravels when lexicographic complexity costs are added, and the distance between this outcome and the most efficient achievable outcome under this concept increases as the discount factor falls. These studies demonstrate that the standard folk theorem results may not hold and that cooperation can suffer when the analysis accounts for only minimal strategic complexity costs. The evolutionary fitness of repeated game strategies played by

ﬁnite automata has also been studied analytically and computationally with results suggesting that strategic complexity costs are an important factor in determining repeated game outcomes.7 In light of the theoretical literature, there is a need for empirical evidence to inform further research dealing with the implications of strategic complexity costs.

7Binmore and Samuelson (1992) consider an evolutionary model of the indefinitely repeated prisoner’s dilemma played by finite automata with lexicographic complexity costs and find that the equilibrium automata reach the efficient cooperative equilibrium. Cooper (1996) finds that a folk theorem result is restored with a different definition of evolutionary stability and finite complexity costs. In contrast with these results, Volij (2002) shows that with lexicographic complexity costs in an evolutionary setting, the only stochastically stable automaton is the one-state automaton which always defects. A simulation by Ho (1996) finds that convergence towards cooperation depends critically on the specification of complexity costs. In particular, he finds that a cost associated with the number of states in the automaton harms cooperation, but a cost associated with the number of state transitions does not. In contrast, a simulation by Linster (1992) using a different algorithm and smaller strategy space shows convergence towards cooperation, with Grim Trigger as the most successful automaton strategy.

8 1.3 Experimental Design

The experiment includes four treatments. Each treatment uses two of the four payoﬀ tables shown in Figure 1.1, which are symmetric, 3x3 versions of the prisoner’s dilemma. To the standard 2x2 prisoner’s dilemma, I add a third “dummy” action (action 2 in tables X and Y, action 1 in table Z and action 3 in table Z’), which is always strictly dominated by the defect action and weakly dominated by the cooperate action. Treatments NOSWITCH and NOSWITCH-R use tables X and Y, treatment SWITCH-C uses Y and Z, and treatment

SWITCH-D uses Y and Z’. Payoﬀs are denominated in experimental currency units (ECUs) where 1 ECU = $0.004. Of the two in use in a particular treatment, one table is randomly chosen to apply in each stage of a repeated game, and the chosen table is publicly announced before the stage begins.

Each session is split into two phases, I and II. In each phase, subjects participate in a series of seven rounds of indeﬁnitely repeated prisoner’s dilemma games. They are matched with the same opponent for the duration of each repeated game, and matches are determined randomly and independently of matches in previous games. In phase I of NOSWITCH,

SWITCH-C and SWITCH-D, subjects participate in a single repeated game in each round. In phase II of these treatments, subjects participate simultaneously in four separate indeﬁnitely repeated prisoner’s dilemma games in each round with a randomly and independently drawn opponent in each game. The order is reversed in NOSWITCH-R, so that multiple games are played in phase I rounds and single games in phase II rounds. Table 1.1 summarizes the features of each treatment.

The continuation probability in each stage of a repeated game is 80%, for an expected game length of ﬁve stages. All repeated games in a given round have the same length. The number of stages in each round were drawn randomly before conducting the sessions, and

9 Figure 1.1: Payoﬀ Tables

the same round lengths are used in each session to control for the inﬂuence of repeated game

length on behavior. Table 1.2 shows the number of stages in each round.

Because the purpose of this experiment is to look for evidence of the impact of strategic

complexity costs on cooperation, the parameters of the game are set to encourage a moderate

level of baseline cooperation. Cooperation through the use of Grim Trigger and Tit-for-Tat

strategies is an equilibrium, and these strategies are risk-dominant compared to a strategy

of Always Defect.8

8Dal Bo and Frechette (2011a) report 61.1% first stage cooperation and 58.7% overall cooperation in a treatment with paramaters similar to mine (the δ = 3/4, R = 40 treatment in their paper). They find that a cooperative equilibrium is a necessary but not sufficient condition for cooperative behavior, but their results indicate that players are more likely to cooperate as the basin of attraction of cooperative strategies grows larger. As defined by Myerson (1991), the resistance parameter representing the basin of attraction of a 1 cooperative vs. a selfish strategy for this experiment is λ = 26 , where λ close to zero favors cooperation and λ close to one favors defection.

10 Table 1.1: Treatments Treatment Payoﬀ Tables Phase I Games/Rd. Phase II Games/Rd. NOSWITCH X and Y 1 4 SWITCH-C Y and Z 1 4 SWITCH-D Y and Z’ 1 4 NOSWITCH-R X and Y 4 1

Subjects in each treatment can see both possible payoff tables on their instructions at all times,9 but which of the two payoff tables applies in a given stage is not always visible on their computer screens. Subjects are allowed to take notes on paper, but they are not told to do so.10 Before the beginning of each repeated game, subjects are told which of the two payoff tables applies in the first stage. They are then presented with a series of three screens in each stage of a game.11 The first12 asks for an action choice (1, 2 or 3) in the current stage, but the payoff table that applies in that stage is not shown at this time. The second screen13 announces which of the two payoff tables will apply in the next stage if the game continues to the next stage. Finally, the third screen14 reports the opponent’s action in the current stage. Because the payoff table that applies in a given stage is announced before the stage begins and not shown when choices are entered, strategies that condition action choices on the payoff table announcement require additional information processing. The payoff table that applies in the next stage is revealed before the opponent’s action in

9See Appendix A for the instructions given to subjects. The experimental software is programmed in zTree (Fischbacher, 2007). 10Notes taken by subjects are not incorporated into the data, but roughly 50-60% of subjects in each treatment appeared to take notes as a memory aid. 11Each of the three stage screens is viewable for a maximum of 20 seconds in both the single and multiple games phases, for a total time limit of 60 seconds per stage. 12See Figure A.5 in Appendix A. 13See Figure A.6 in Appendix A. 14See Figure A.7 in Appendix A.

11 Table 1.2: Repeated Game Lengths Round Trial 1 2 3 4 5 6 7 8 9 10 11 12 13 14 # of Stages 5 4 2 6 1 8 7 4 1 3 10 3 3 4 1 Mean # of Stages All Rounds: 4.1 Phase I: 4.6 Phase II: 3.6 Repeated game lengths for rounds 1-7 and rounds 8-14 are reversed for NOSWITCH-R. Each session began with a 5-stage trial round which did not count towards payments.

the current stage so that strategies which condition on opponent behavior require contingent planning. The multiple games phase of each treatment proceeds similarly to the single games phase, except that subjects participate in four simultaneous repeated games in each round.15 The games are labeled “Blue,” “Green,” “Red” and “Yellow,” and the position of each color on the screen remains the same throughout the multiple game phase. Payoﬀ tables are drawn randomly and independently for each color in each stage.

1.4 Research Questions

Question 1: Compared to the baseline, is less cooperation observed when the cooperate action is state-dependent?

Payoff table switching is present in a trivial way in the NOSWITCH baseline to maintain the overall structure of the experiment across treatments, so it should not affect behavior in this treatment. In both of its payoff tables (X and Y), the cooperate action is 1, the dummy action is 2 and the defect action is 3, so the action to take in each stage for a given strategy is the same for both tables. The tables differ only in the payoff if the action profile (2,2) is selected, but action 2 is strictly dominated by defect and weakly dominated by cooperate

15See Figures A.8-A.10 in Appendix A.

12 in both tables, so the complexity of any rational strategy is identical in this treatment to what it would be in a two-by-two prisoner’s dilemma. In SWITCH-C, however, choosing the correct cooperate action requires players to account for payoff table switching because the cooperate action is action 1 in table Y and action 2 in table Z. If one thinks of payoff table switching as random changes in the state of nature, one can say that the cooperate action is state-dependent in this treatment, while the defect action is not because it is action 3 in both tables. Because the cooperate action is state-dependent, using a punishment-enforced cooperative strategy in SWITCH-C requires a player to monitor her opponent’s actions and account for payoff table switching so that the correct cooperate action can be chosen in each stage. Only monitoring of the opponent’s actions is necessary in NOSWITCH. Hence, implementing a cooperative strategy in SWITCH-C is more complex because it requires an extra step of information processing which is not necessary in NOSWITCH.

Question 2: Compared to the baseline, how is cooperation aﬀected when the defect action is state-dependent?

In SWITCH-D, choosing the correct defect action requires players to account for payoff table switching because the defect action is action 3 in table Y and action 2 in table Z’. Hence, one can say that the defect action is state-dependent in this treatment, while the cooperate action is not because it is action 1 in both tables. If cooperation is affected when the cooperate action is state-dependent, making the defect action state-dependent instead may also affect cooperation because it increases the implementation complexity of punishment-enforced cooperative strategies. Using such a strategy in SWITCH-D requires a player to monitor her opponent’s actions and account for payoff table switching so that the correct defect action can be chosen if the opponent has defected and punishment is necessary. In NOSWITCH, these strategies only require monitoring of the opponent.

13 It is also important to rule out the possibility that effects observed in SWITCH-C are simply due to framing, i.e., that permutations of the payoff table make the cooperate or defect action more salient, which could make the action more or less likely to be chosen. Because payoff table switching affects the defect action instead of the cooperate action in SWITCH-D, framing reasons for reduced cooperation in SWITCH-C should produce the opposite effect in SWITCH-D.

Question 3: Compared to isolated single games, is cooperation aﬀected when subjects play multiple games simultaneously?

To provide a richer investigation of the cognitive costs of strategic complexity, I introduce a second source of cognitive cost to the experiment by including rounds in which subjects play multiple games simultaneously. In the multi-market duopoly game of Fershtman and Kalai (1993), firms active in multiple markets with an upper bound on the complexity of their overall strategy must use simpler strategies in each market. If such diseconomies of scale in strategic implementation are present in this experiment, subjects may be more likely to use a simple selfish strategy in individual games of multiple game rounds in order to reduce the overall cognitive cost.16 Also, the results of Cason et al. (2010), Cason and Gangadharan (2010), Savikhin and Sheremeta (2010) and Bednar et al. (2012) suggest that the cognitive cost of strategic implementation in multiple simultaneous games can be reduced if the same strategy is used in multiple games.17 If I find that subjects mix between

16Subjects may also deal with the additional cognitive cost of of playing multiple games by adopting global strategies which prescribe the same action in all four games in each stage, conditional on their joint history. A global grim trigger strategy, for example, initially cooperates in all four games and responds to defection by any opponent by defecting in all four forever. This type of strategy is less complex than an overall strategy which separately conditions actions in each of the four games on the opponent’s actions in that particular game, and it is also likely to result in fewer cooperative outcomes in individual games. 17In contrast, Hauk and Nagel (2001) and Hauk (2003) find that individual subjects mix between cooperative and selfish strategies when playing multiple finitely repeated prisoner’s dilemmas simultaneously.

14 selfish and cooperative strategies in simultaneous NOSWITCH games, then less mixing in SWITCH-C and SWITCH-D would be consistent with findings of this literature. Because strategies are more complex to implement in individual games of these treatments, subjects should be less likely to mix between strategies in them than in the baseline due to the greater cognitive cost. Dal Bo (2005), Camera and Casari (2009), Duffy and Ochs (2009) and Dal Bo and Frechette (2011a) find evidence that subjects learn to cooperate over a series of indefinitely repeated prisoner’s dilemma games in which cooperation is supportable in equilibrium, as it is here. Hence, it may be that the additional cognitive cost of strategic implemention in multiple games makes relatively complex cooperative strategies less attractive in phase II than in phase I of NOSWITCH, SWITCH-C and SWITCH-D, but that this effect is mitigated by learning to cooperate over the course of a session. The NOSWITCH-R treatment is included as a control for the effect of learning in phase I on phase II behavior in the other treatments. Comparison of phase I results of this treatment with those of NOSWITCH allows me to control for learning by comparing results of the multiple games phase to a parallel single games phase.

1.5 Results

The experiments were conducted at the Ohio State University Experimental Economics Lab in the winter and spring of 2011. A total of 136 subjects participated in the experiment over eight sessions, with two sessions and 34 subjects per treatment. Subjects were recruited via email invitations sent out randomly to students in a large database of Ohio State undergraduates of all majors. Sessions lasted between 60 and 90 minutes, and average earnings were $18.85.

15 1.5.1 Aggregate Cooperation

I measure aggregate overall cooperation as the percentage of all action choices which are cooperative. I also study the aggregate cooperation rate in the first stages of repeated games only, which gives a view of players’ intentions at the start of a repeated game before they observe actions of their opponents and thus indicates what type of strategy they adopt. Figure 1.2 shows the frequencies of overall and first stage cooperation by round for NOSWITCH, SWITCH-C and SWITCH-D. Changes in overall cooperation between rounds are quite consistent across treatments. There is a statistically significant correlation between the overall cooperation in a repeated game and the length of the game in all three of these treatments.18 This correlation is not unexpected, as cooperation will stabilize in some subject pairs over the course of a repeated game but unravel in others. In comparison, the frequency of first stage cooperation is relatively stable across rounds.19 Aggregate overall cooperation and first stage cooperation by treatment and phase are reported in Table 1.3.20 The distributions of stage outcomes on the payoff table for all four treatments are reported in Table 1.4. The frequency of choosing dummy actions was less than 3% for all treatments, confirming that subjects had a sufficient understanding of the game and the software interface.

18The correlation coefficents and p-values for Spearman rank-order tests are as follows. NOSWITCH: r = -.6623, p = .0099. SWITCH-C: r = -.8818, p < .0001. SWITCH-D: r = -.7715, p = .0012. 19The dramatic dip in overall cooperation between rounds eight and ten of each treatment is noteworthy because it marks the beginning of phase II, when subjects are adjusting to playing multiple games. However, this appears to be due to the length of round ten (ten stages, the longest of the repeated game lengths used) because a similar dip in cooperation is not observed for first stage actions. 20I assess the significance of differences in aggregate cooperation between treatments using a probit regression with an indicator variable for one of the treatments and standard errors clustered at the session level. A Wilcoxon-Mann-Whitney test yields similar results for significance of differences between treatments.

16 Figure 1.2: Cooperation by Round

Overall 1st Stage

Result 1: Compared to the baseline, less cooperation is observed when the cooperate action is state-dependent.

Compared to phase I of the NOSWITCH baseline,21 I observe significantly less first stage cooperation in phase I of SWITCH-C, where the cooperate action is state-dependent. I also observe less first stage cooperation in SWITCH-C than in NOSWITCH during phase II, and though the difference is not statistically significant, its magnitude of 9.4 percentage points is noteworthy. I also observe less overall cooperation in both phases of SWITCH-C, but these differences are not statistically significant. This result indicates that increasing the implementation complexity of cooperative strategies through a state-dependent cooperate action makes subjects less likely to use cooperative

21The 55.5% rate of ﬁrst stage cooperation observed in phase I NOSWITCH games is close to the 61.1% rate observed by Dal Bo and Frechette (2011a) in their δ = 3/4, R = 40 treatment, which used comparable parameters according to the cooperation indices of Murnighan and Roth (1983).

17 Table 1.3: Frequency of Cooperation All Stages 1st Stage Phase III III NOSWITCH 40.6% 40.2% 55.5% 60.0% SWITCH-C 35.3% 34.5% 41.6%** 50.6%

SWITCH-D 29.5%*** <<< 33.7%*** 42.4%*** 46.8%***

NOSWITCH-R 36.6% <<< 57.8%*** 43.4%** <<< 64.7% Diﬀerence from NOSWITCH signiﬁcant at: *** .01 level, ** .05 level, * .1 level.

Diﬀerence between phases signiﬁcant at: <<<.01 level, <<.05 level, <.1 level.

strategies.22 In terms of the finite automata model, cooperative strategies are more complex in SWITCH-C because more states are needed for an automaton to implement such strategies than in NOSWITCH. Because cooperative actions in SWITCH-C are conditional on the payoff table announced in a given stage, which can be thought of as the action of a third player (nature), the state transition functions of these strategies take the payoff table announcement as an input in addition to the current state and the opponent’s action, and additional automaton states are needed to choose actions conditional on this announcement. Always Cooperate (AC) requires two automaton states instead of one, Grim Trigger (GT) requires three states instead of two, and Tit-for-Tat (TFT) requires four states instead of two. Always Defect (AD), however, requires only one state in both NOSWITCH and SWITCH- C.23 I find that subjects are less likely to adopt a cooperative strategy in SWITCH-C than in

22It is important to acknowledge that implementing a complex strategy may be more cognitively costly for some subjects than for others. If subjects realize that such heterogeneity in complexity costs exists, they may base their strategy choice on the expected complexity costs of their opponents as well as their own costs. A subject may always defect because implementing a complex cooperative strategy is too costly for her, or because she is best-responding to the expectation that cooperating is too costly for her opponent. Beliefs about the opponent’s likelihood of adopting a cooperative strategy should matter more in the relatively complex strategic environment of SWITCH-C than in the simple one of NOSWITCH, where it is more likely to be common knowledge that strategic complexity costs do not prohibit cooperation. For this reason, increased cognitive cost of implementing cooperative strategies may reduce the propensity to cooperate in SWITCH-C indirectly as well as directly. 23See Appendix A for directed graph representations of the minimal ﬁnite automata implementing these strategies in each treatment.

18 Table 1.4: Summary of Stage Outcomes

NOSWITCH, which suggests that the cognitive cost of increased implementation complexity indeed aﬀects strategy choice.

Result 2: Compared to the baseline, less cooperation is observed when the defect action is state-dependent.

I observe significantly less overall and first stage cooperation in SWITCH-D than in NOSWITCH for both phases I and II. This result indicates that increasing the implementation complexity of punishment-enforced cooperative strategies through a state-dependent defect action reduces cooperation. Making the defect action state-dependent increases the complexity of a punishment-enforced cooperative strategy because using such a strategy requires a player to monitor her opponent and account for payoff table switching so that the

19 correct defect action can be chosen if the opponent is to be punished. Only monitoring of the opponent is necessary in NOSWITCH. However, AD is also a more complex strategy in this treatment than in NOSWITCH because a player must account for payoff table switching to choose the correct defect action in each stage. According to the finite automata model, GT and TFT require four states in SWITCH-D instead of the two states required in NOSWITCH, and AD requires two states instead of one.24 Hence, the observed fall in cooperation suggests an upper bound on strategic complexity because it appears that what matters is not only the relative complexity of available strategies but also the absolute level of complexity of cooperative strategies. Alternatively, the cognitive costs of implementation complexity may be convex so that as both cooperative and selfish strategies become more complex, cooperation falls because the increase in cognitive cost is more dramatic for the relatively complex cooperative strategies. Because cooperation falls in both SWITCH-C and SWITCH-D relative to the baseline, it is reasonable to rule out the possibility that the primary treatment effects are due to framing, i.e., that permutations of the payoff table make the cooperate or defect action more salient, which makes the action more or less likely to be chosen. This influence would have opposite effects on cooperation in SWITCH-C and SWITCH-D. Instead, I observe that both treatments reduce cooperation compared to the baseline, indicating that framing is not the primary source of the treatment effects. However, there is evidence that some subjects who cooperate in SWITCH-C attempt to use payoff table switching as a coordination device. Compared to phase I of SWITCH-C, I observe slightly more first stage cooperation but less overall cooperation in phase I of SWITCH-D, although these differences are not statistically significant. This discrepancy appears because, of the subjects in phase I of SWITCH-C who cooperated but whose opponents defected in the first stage of a game, 41.2% chose to cooperate again in the second stage, while only 24.1% of their counterparts in phase I of

24See Appendix A for directed graph representations of the minimal ﬁnite automata implementing these strategies.

20 NOSWITCH and 29.4% in SWITCH-D did so.25 This result suggests that the cooperative strategies subjects adopt tend to be more lenient in SWITCH-C than in other treatments, perhaps signaling a desire to coordinate on the state-dependent cooperate action.

Result 3: Cooperation does not decrease when subjects participate in multiple simultaneous games after the single game phase. However, less cooperation is observed when multiple games are played in a phase than when single games are played in a parallel phase.

The frequencies of overall and first stage cooperation do not decrease significantly when moving from the single game to multiple game phases of NOSWITCH, SWITCH-C and SWITCH-D. Indeed, there is evidence that cooperation increases between phases (overall cooperation increases significantly between phases I and II of SWITCH-D), consistent with results of other experiments which suggest that subjects learn to cooperate over the course of a session.26 Figure 1.3 shows levels of overall and first stage cooperation by round for NOSWITCH, where single games are played in phase I and multiple games in phase II, and NOSWITCH- R, where the order of single and multiple games phases is reversed. Comparing the results of these treatments provides evidence that the cognitive cost of playing multiple simultaneous games leads to less cooperation than in isolated single games. I observe significantly less first stage cooperation in NOSWITCH-R than in NOSWITCH during phase I, suggesting that relatively inexperienced subjects are less likely to use cooperative strategies in multiple simultaneous games than in isolated single games. The difference in overall cooperation is similar but not statistically significant. In phase II, less first stage and overall cooperation is observed in NOSWITCH than in NOSWITCH-R, although the difference is statistically

25A one-tailed t-test indicates that the difference between SWITCH-C and NOSWITCH is significant (p-value = .0306), but the difference between SWITCH-C and SWITCH-D is not (p-value = .1069). 26See Dal Bo (2005), Camera and Casari (2009), Duffy and Ochs (2009) and Dal Bo and Frechette (2011a).

21 Figure 1.3: Cooperation by Round: NOSWITCH/NOSWITCH-R

Overall 1st Stage

significant only for overall cooperation. This result indicates that after gaining experience, subjects are more likely to stabilize on cooperation when playing isolated single games than when playing multiple simultaneous games. This result is consistent with a finite automata interpretation of costly strategic complexity. If a single automaton must be used to implement strategies in all four simultaneous games, less cooperation is predicted in the multiple games phase than in the single games phase because complex strategies are less likely to be used in each individual game of the multiple games phase. In phase II of NOSWITCH, the number of automaton states needed to enforce cooperation independently in each of n individual games would be at least 2n. However, implementing an AD strategy in some games does not require any additional states because it prescribes a constant action unconditional on history. Only one state is needed to implement AD in all four games simultaneously. The increase in both overall and first stage cooperation between phases I and II of NOSWITCH-R is large and statistically significant. Hence, when the number of games

22 per round decreases between phases I and II instead of increasing as in the other treatments, it appears that subjects learn to cooperate. This result supports the idea that in phase II of the other treatments, there is negative impact on cooperation due to the cognitive cost of playing multiple games that is mitigated by learning to cooperate over the course of a session. It also suggests that if subjects were to play single games instead of multiple games in phase II of these treatments, the increase in cooperation over the course of these sessions would be more pronounced.

1.5.2 Strategy Inference

This study is concerned with the importance of complexity in strategy choice, so aggregate results do not tell the whole story. Subjects’ underlying strategies can be inferred from their observed actions by a maximum likelihood technique developed by El-Gamal and Grether (1995) and extended to repeated game applications by Engle-Warnick and Slonim (2006) and Engle-Warnick et al. (2007). This technique measures the proportion of each subject’s observed actions that can be explained by candidate repeated game strategies and estimates the prevalence of each candidate strategy by maximizing a log-likelihood function summing across all subjects and strategies. Table 1.5 describes the 20 candidate strategies considered in this analysis.27 This technique has been used by Aoyagi and Frechette (2009), Camera et al. (2010), Dal Bo and Frechette (2011a, 2011b) and Fudenberg et al. (2012) to infer strategies from observed actions in their repeated prisoner’s dilemma experiments.

27The candidate strategies considered here are the same as those used by Fudenberg et al. (2012) in analyzing their experiment on prisoner’s dilemmas with exogenously imposed noisy implementation of intended actions. The names and abbreviations of some candidate strategies diﬀer from those used in Fudenberg et al. (2012). Results of that study indicate that players adopt more lenient punishment strategies when their opponents’ intentions are not perfectly revealed by their observed actions. Though my experiment does not involve exogenously noisy implementation, I consider the same set of candidate strategies because the increased complexity of implementing strategies in this experiment may cause subjects to make errors. Recognizing that possibility, subjects may use more lenient strategies, as they do in Fudenberg et al. when errors are exogenous. However, lenient strategies also require more memory and contingent planning, so the increased complexity treatments of this experiment may discourage subjects from adopting them.

23 Table 1.5: Candidate Automaton Strategies

Strategy Abbreviation Description Always Cooperate AC Cooperate in every stage. Tit-for-Tat TFT Cooperate unless opponent defected in last stage. Tit-for-2-Tats TF2T Cooperate unless opponent defected in both of last 2 stages. Tit-for-3-Tats TF3T Cooperate unless opponent defected in all of last 3 stages. 2-Tits-for-1-Tat 2TFT Cooperate unless opponent defected in either of last 2 stages. 2-Tits-for-2-Tats 2TF2T Cooperate unless opponent defected twice consecutively in 2 of last 3 stages. 2-Stage Trigger T2 Cooperate until opponent defects, then defect for 2 stages. Grim Trigger GT Cooperate until opponent defects, then defect forever. Forgiving Trigger FT Cooperate until opponent defects in 2 consecutive stages, then defect forever. Twice-Forgiving Trigger 2FT Cooperate until opponent defects in 3 consecutive stages, then defect forever. Win-Stay Lose-Shift WSLS Cooperate if both players chose same action in last stage, otherwise defect. 2-Stage Win-Stay Lose-Shift WSLS2 Cooperate if both players chose same action in last 2 stages, otherwise defect. Always Defect AD Defect in every stage. Cooperate-Defect CD Cooperate in stage 1, then defect forever. Selfish TFT STFT Defect in stage 1, then play TFT. Selfish TF2T STF2T Defect in stage 1, then play TF2T. Selfish TF3T STF3T Defect in stage 1, then play TF3T. Selfish GT SGT Defect in stage 1, then play GT. Selfish FT SFT Defect in stage 1, then play FT. Alternate ALT Defect in stage 1, then alternate between cooperating and defecting.

The maximum likelihood technique works as follows. Each subject is assumed to use the same strategy in each repeated game of a phase.28 In each stage of a repeated game, there is some probability that a subject deviates from the action prescribed by the chosen strategy. In stage t of repeated game r, I assume that subject i who uses strategy sk cooperates

k k if the indicator function yirt(s ) = 1{sirt(s ) + γirt ≥ 0} takes a value of 1 and defects

k k otherwise, where sirt(s ) is the action prescribed by strategy s (1 for cooperate and -1 for defect) given the history of repeated game r up to stage t, is the error term, and γ is the variance of the error. The likelihood function of strategy sk for subject i has the logistic 1 1 k Y Y yirt 1−yirt form pi(s ) = ( k ) ( k ) . The resulting log- 1 + exp(−sirt(s )/γ) 1 + exp(sirt(s )/γ) R T X X k k likelihood function has the form ln( p(s )pi(s )), where K is the set of candidate I K strategies s1, ..., sK and p(sk) is the proportion of the data explained by sk. The entire sequence of actions in a phase is observed for each subject, and the log-likelihood function

28Results of the probit regression reported in Table 1.7 of Section 1.5.3 indicate that this assumption is reasonable because whether subjects cooperate in a repeated game is found to depend heavily on their choices in previous repeated games.

24 Table 1.6: Maximum Likelihood Estimates of Strategy Prevalence

Treatment NOSWITCH SWITCH-C SWITCH-D NOSWITCH-R Phase I II I II I II I II AC 0.03 0 0 0.03 0 0.03 0.06 0 (0.03) (0) (0) (0.03) (0) (0.03) (0.06) (0) TFT 0.08 0.16* 0.08 0.11* 0.18 0.22*** 0.23* 0.39*** (0.07) (0.09) (0.07) (0.06) (0.12) (0.08) (0.14) (0.11) TF2T 0 0.05 0 0.11* 0 0.10* 0.04 0.13 (0) (0.05) (0.01) (0.06) (0.01) (0.06) (0.04) (0.12) TF3T 0 0.06 0 0 0 0 0.02 0.03 (0.02) (0.04) (0) (0.02) (0.02) (0) (0.02) (0.03) 2TFT 0 0.14 0.05 0 0 0.06 0 0 (0) (0.13) (0.07) (0.01) (0.03) (0.05) (0) (0.04) 2TF2T 0.04 0 0 0 0.04 0 0.02 0.04 (0.06) (0.06) (0.05) (0.02) (0.03) (0) (0.03) (0.09) T2 0 0.04 0 0 0 0 0 0 (0) (0.03) (0) (0) (0) (0) (0) (0) GT 0.24** 0.14 0.10* 0.18* 0.07 0.04 0.05 0.07 (0.10) (0.11) (0.06) (0.09) (0.06) (0.06) (0.05) (0.08) FT 0.09 0 0.11 0 0.04 0 0 0 (0.08) (0.01) (0.07) (0.03) (0.03) (0) (0) (0.02) 2FT 0 0 0.04 0.01 0.03 0 0.02 0 (0.02) (0.01) (0.04) (0.02) (0.02) (0) (0.01) (0.02) WSLS 0.02 0 0 0 0 0 0 0 (0.05) (0) (0) (0) (0) (0) (0) (0) WSLS2 0 0.02 0 0 0 0.02 0 0 (0) (0.02) (0) (0) (0) (0.03) (0) (0) AD 0.26*** 0.29*** 0.42** 0.45*** 0.48*** 0.47*** 0.43*** 0.18*** (0.08) (0.07) (0.16) (0.09) (0.09) (0.08) (0.12) (0.06) CD 0.06 0.03 0 0.05 0.03 0 0.05 0 (0.05) (0.03) (0) (0.05) (0.03) (0) (0.04) (0) STFT 0.18** 0.04 0.07 0.06 0.13* 0.06 0.10 0.11* (0.07) (0.03) (0.07) (0.04) (0.07) (0.04) (0.11) (0.06) STF2T 0 0 0.09 0 0 0 0 0 (0.03) (0) (0.08) (0) (0) (0.01) (0) (0) STF3T 0 0 0 0 0 0 0 0 (0) (0) (0.01) (0) (0) (0) (0) (0.02) SGT 0 0.03 0.04 0 0 0 0 0.03 (0.02) (0.02) (0.06) (0) (0) (0.01) (0.01) (0.03) SFT 0 0 0 0 0 0 0 0.03 (0) (0) (0) (0) (0) (0) (0) (0.02) ALT 0 0 0 0 0 0 0 0 (0) (0) (0) (0) (0) (0) (0.01) (0) Bootstrapped standard errors are in parentheses below estimates. Wald test: significant estimates in bold. *** significant at .01 level; ** significant at .05 level; * significant at .1 level.

25 is maximized to estimate the proportion of the data in the phase which is explained by each candidate strategy. The results are reported in Table 1.6.

Result 4: Compared to the baseline, cooperative strategies are less prevalent and Always De- fect is more prevalent in treatments where cooperative strategies are more complex.

The maximum likelihood estimates indicate that cooperative strategies are less prevalent while selfish strategies are more prevalent in SWITCH-C and SWITCH-D than in NOSWITCH. The sums of the NOSWITCH estimates for cooperative strategies29 are 51% for phase I and 62% for phase II, while for SWITCH-C and SWITCH-D, respectively, they are 39% and 36% for phase I and 45% and 47% for phase II. The estimated prevalence of Always Cooperate (AC) is zero or not significantly different from zero in all treatments, confirming that subjects do not cooperate unconditionally but use punishment-enforced cooperative strategies. The estimated prevalence of the simple AD strategy is 16 to 22 percentage points greater in SWITCH-C and SWITCH-D than in NOSWITCH in both phases, and all of these differences in the prevalence of AD are statistically significant except for the difference between NOSWITCH and SWITCH-C in phase I.30 These estimates confirm that the complexity treatments make subjects more likely to adopt a simple selfish strategy instead of a cooperative strategy than in the baseline environment. Results of this analysis also reveal that cooperative strategies are less prevalent and AD is more prevalent when multiple games are played in phase I (NOSWITCH-R) than when single games are played in phase I or when multiple games are played in phase II (NOSWITCH). Cooperative strategies are estimated to account for 51% of phase I data and 62% of phase II

29Speciﬁcally, the strategies I refer to as cooperative strategies are those by which it is possible that the subject cooperates in every stage of any given repeated game. 30One-tailed t-tests for samples with unequal variances yield the following p-values: NOSWITCH vs. SWITCH-C, phase I: .1872; NOSWITCH vs. SWITCH-D, phase I: .0361; NOSWITCH vs. SWITCH-C, phase II: .0826, NOSWITCH vs. SWITCH-D, phase II: .0476.

26 data in NOSWITCH but only 44% of the phase I data in NOSWITCH-R. AD is estimated to account for 26% of phase I data and 29% of phase II data in NOSWITCH, while it is estimated to account for 43% of the phase I NOSWITCH-R data. These differences are not statistically significant, but their magnitudes are large enough to suggest that subjects play more selfishly when faced with the greater cognitive cost of playing multiple simultaneous games in phase I than when playing single games in phase I or multiple games in phase II, when they have more experience. The NOSWITCH-R estimates also support the aggregate results suggesting that subjects learn to cooperate over the course of a session. The large increase in aggregate cooperation between phases I and II of this treatment is accompanied by a large and significant (p-value = .0335) decrease in the estimated prevalence of AD (from 43% to 18%) between phases. The estimated prevalence of TFT increases from 23% to 39% between phases I and II, but this difference is not statistically significant (p-value = .1861). In phase I of NOSWITCH, SWITCH-C and SWITCH-D, the estimated prevalence of TFT is relatively low (8-18%) and, according to a Wald test, not significantly different from zero. However, comparing the phase I and II estimates indicates that subjects learn to play TFT over the course of a session, as the estimates are larger (16-22%) and significant in phase II of these treatments.31 The above evidence indicates that subjects learn to use TFT over the course of a session, but that the increase in cooperation between phases I and II of NOSWITCH, SWITCH-C and SWITCH-D is less striking than in NOSWITCH-R. This result suggests that cooperation

31Given the evidence that subjects learn to play TFT over the course of a session, it is interesting that NOSWITCH-R is nonetheless the only treatment with a phase I TFT estimate significantly greater than zero (23%). A look at the individual action level reveals that subjects learn to play TFT within phase I of NOSWITCH-R, which includes four times the number of repeated games played in phase I of the other three treatments. Of the 408 individual game-histories in rounds 1-3 of NOSWITCH-R, 82 (20.1%) of them are consistent with TFT. This prevalence of TFT is comparable to that observed in phase I of the NOSWITCH baseline, where 56 of 238 histories (23.5%) are consistent with TFT. However, of the 544 histories in rounds 4-7 of NOSWITCH-R, 181 (33.3%) are consistent with TFT. According to a Wilcoxon signed-ranks test, this is a significant increase from the prevalence of TFT in the first three rounds of NOSWITCH-R (p-value = .0044). Hence, it appears that subjects learn to play TFT over the course of Phase I of NOSWITCH-R, which suggests that learning to play TFT is a function of not only the number of rounds played but also the number of repeated games played.

27 would increase further in phase II of these treatments if not for the increased cognitive cost of playing multiple simultaneous games.32 In their experiments on multiple simultaneous games, Bednar et al. (2012) find evidence of strategy spillovers between repeated prisoner’s dilemmas and other repeated games played simultaneously.33 Their data also suggest that behavioral spillovers between games are stronger when the games are individually more cognitively demanding. Consistent with this result, I find that subjects are more likely to use the same type of strategy in simultaneous games in treatments where strategies are more complex.34 In terms of the finite automaton model, all of the strategies with significant estimated prevalence have the least complexity in NOSWITCH and NOSWITCH-R, while AD and GT are less complex in SWITCH-C than in SWITCH-D. Restricting attention to first stage actions only, I find that subjects cooperate in one, two or three of the four simultaneous games in 29.4% and 31.9% of multiple game rounds in NOSWITCH and NOSWITCH-R, respectively, compared to frequencies of 25.2%

32Interestingly, the Tit-for-2-Tats (TF2T) strategy explains a significant proportion of the data in phase II of SWITCH-C and SWITCH-D. This is a more complex but more lenient version of TFT, suggesting that some subjects account for the fact that opponents may make mistakes in implementing strategies due to the greater complexity in these treatments. Alternatively, subjects using TF2T may forgive a defection by their opponents in an effort to signal their desire to coordinate. As reported in Section 1.5.1, subjects who cooperate in the first stage in SWITCH-C are more likely to forgive defection by opponents in the first stage than their counterparts in SWITCH-D. Accordingly, of the subjects who implement a reciprocal cooperative strategy in these treatments, a greater proportion are estimated to use a lenient version (TF2T) in SWITCH-C than in SWITCH-D. Forgiving Trigger (FT), a more lenient version of Grim Trigger, is also estimated to have a greater prevalence in SWITCH-C than SWITCH-D, but the estimate is not significantly greater than zero according to a Wald test. 33In contrast, Hauk and Nagel (2001) and Hauk (2003) find that subjects mix between different types of strategies in simultaneous games. 34I do not find evidence that subjects use a global trigger strategy to economize on implementation complexity across multiple simultaneous games. Of all individual round-histories of subjects’ and opponents’ actions in multiple game rounds of more than one stage, the percentage of them that are consistent with a global trigger strategy is 3.5% for NOSWITCH, 1.2% for SWITCH-C, 5.9% for SWITCH-D and 0.0% for NOSWITCH-R.

28 in SWITCH-C and 15.5% in SWITCH-D.35 This evidence supports the idea that the cognitive cost of strategic implementation in multiple simultaneous games is reduced if subjects use the same type of strategy in these games.

1.5.3 Regression Analysis

To check the robustness of the observed impact of increased complexity on aggregate cooperation, I conduct probit regressions to study how the choice to cooperate is influenced by the complexity treatments and other possible explanatory variables. These regressions include the choice to cooperate in phase I single game rounds as the binary dependent variable and explanatory variables including SWITCH-C and SWITCH-D dummies and features of the history of play which may systematically affect cooperation.36 The subject’s action (1 if cooperate and 0 otherwise) in the first stage of the previous repeated game and the first stage of the first repeated game are included because they should be strongly correlated with the subject’s decision in the current game if subjects use the same type of strategy in all games. The action of the subject’s opponent in the first stage of the previous repeated game and the first stage of the first repeated game are included to control for contagion effects. Because aggregate cooperation is negatively correlated with the number of rounds in a repeated game (see Section 1.5.1), I also include the number of rounds in the previous repeated game to control for any lagged effect of repeated game length on cooperation. Table 1.7 shows the results of probit regressions for cooperation in any stage of rounds 2-7 and for cooperation in the first stages of these rounds only.

35According to a one-tailed t-test, the difference between NOSWITCH and SWITCH-C is not statistically significant (p-value = .1517), but the difference between NOSWITCH-R and SWITCH-C is (p-value = .0523). The frequencies of mixing between cooperative and selfish first stage actions in NOSWITCH, NOSWITCH-R and SWITCH-C are all significantly greater than the frequency in SWITCH-D (p-values of less than .0001 for NOSWITCH/NOSWITCH-R and .0044 for SWITCH-C). 36Data from multiple games phases are excluded from these regressions to eliminate possible interaction effects due to the additional cognitive cost of playing multiple simultaneous games. Data from phase II of

29 Table 1.7: Probits Reporting Marginal Eﬀects of Treatments and History of Play

1st Stage, Rounds 2-7 Any Stage, Rounds 2-7 Dependent Variable: Cooperation in — Coefficient Std. Err. Coefficient Std. Err. SWITCH-C -0.088 (0.059) 0.001 (0.050) SWITCH-D -0.122* (0.069) -0.080 (0.050) Cooperated in First Stage of Previous Rd. 0.496*** (0.050) 0.270*** (0.040) Opponent Cooperated in First Stage of Previous Rd. 0.135*** (0.046) 0.058* (0.034) # of Stages in Previous Rd. 0.019** (0.008) 0.018*** (0.005) Cooperated in First Stage of Rd. 1 0.245*** (0.056) 0.099** (0.043) Opponent Cooperated in First Stage of Rd. 1 0.022 (0.056) -0.037 (0.040) Observations 612 2856 Standard errors clustered at the subject level. *** significant at .01 level; ** significant at .05 level; * significant at .1 level.

Even when controlling for these other influences on cooperation, a treatment effect is observed for first stage actions, indicating that the effect of increased complexity on strategy choice is robust to the inclusion of other variables that explain cooperation. The SWITCH- D treatment effect is statistically significant in this analysis, but the SWITCH-C effect is not. However, the magnitude of the estimated effects of SWITCH-C and SWITCH-D on first stage cooperation are both economically significant because they are consistent with the aggregate frequencies of first stage cooperation observed in these treatments. According to the regression, subjects are about 9 to 12 percentage points less likely to use a cooperative strategy when the complexity of such strategies is increased compared to the baseline, whereas aggregate frequencies of first stage cooperation show a 13 to 14 percentage point difference between the treatments and the baseline (see Table 1.3). Hence, the complexity treatments appear to explain most of the aggregate differences in first stage cooperation when I control for other possible influences on strategy choice. Estimates for actions in any stage of a repeated game are generally consistent with but smaller than for first stage NOSWITCH-R, the single games phase of this treatment, are excluded to eliminate possible confounding effect of learning over the course of a session.

30 actions only, which is expected because actions after the first stage of a game should depend primarily on the behavior of the opponent in the current game. In both of the above regressions, the significant positive effects of the player’s own choices in previous games on her choice to cooperate in the current game indicate that strategy choice is relatively consistent across games. In comparison, the influence of contagion on strategy choice appears to be insubstantial. The marginal effects of the previous opponent’s first stage cooperation on the choice to cooperate in the current game (13.5 percentage points for the first stage and 5.8 percentage points for any given stage) are statistically significant, but they are dominated in magnitude by the effects of the player’s own choices in the previous (49.6 and 27.0) and the first (24.5 and 9.9) repeated game. The effect of the length of the last repeated game on cooperation is significant but small, indicating that for each round in the previous game subjects are about 2 percentage points more likely to cooperate in the current game. If cooperation depends on the cognitive cost of strategic implementation, a positive relationship between cognitive ability and the likelihood of cooperation should exist. To test this hypothesis, I obtained subjects’ consent to request their American College Test (ACT) and Scholastic Aptitude Test (SAT) scores from the Ohio State University registrar’s office. These test scores have been shown by Frey and Detterman (2004) and Koenig et al. (2008) to be strongly correlated with cognitive ability. Nevertheless, this is one of the first studies to use ACT or SAT scores as a measure of cognitive ability in the experimental economics literature.37 ACT scores were obtained for 88 of the 136 subjects who participated in this experiment. SAT scores were obtained for 40 of the remaining 48 subjects, and SAT-ACT concordance scores were used for these subjects.38 Eight subjects were transfer

37Benjamin and Shapiro (2005) study relationships between cognitive ability and decision-making biases, while and Casari et al. (2007) study the eﬀect of cognitive ability on the likelihood of falling victim to the winner’s curse. 38See http://professionals.collegeboard.com/profdownload/act-sat-concordance-tables.pdf for SAT-ACT concordance tables.

31 Table 1.8: ACT and SAT-ACT Concordance Score Summary Statistics Treatment NOSWITCH SWITCH-C SWITCH-D NOSWITCH-R POOLED Subjects 34 34 34 34 136 Median 28 28 27 27 27 Mean 27.97 27.87 27.63 27.41 27.72 Std. Err. 0.719 0.575 0.585 0.650 0.319 with ACT 61.8% 55.9% 64.7% 76.5% 64.7% SAT Only* 35.3% 35.3% 29.4% 17.6% 29.4% No Score 2.9% 8.8% 5.9% 5.9% 5.9% Top 5% 23.5% 14.7% 17.6% 17.6% 18.4%

students who reported neither test score. Summary statistics on the ACT and SAT-ACT concordance scores are reported in Table 1.8. I test for a relationship between cognitive ability and cooperation using probit regressions with the choice to cooperate as the dependent variable and dummies indicating whether a subject has an ACT or SAT-ACT concordance score in the top 5% of all test-takers (18.4% of subjects) or below the top 20% of all test-takers (17.6% of subjects) as explanatory variables. I use ACT percentile as a measure of cognitive ability because ACT scores are based on a rank-order scale and not an additive scale. Other explanatory variables include a dummy for phase II of a treatment and interaction terms for phase II and the score percentile variables. I also include a control variable for subjects reporting no test score, but its estimated coeﬃcient is not meaningful due to the small number of subjects in this category. Table 1.9 shows the results of probit regressions for the choice to cooperate in any stage of a repeated game and in the ﬁrst stage only, with separate regressions for each treatment in both cases.

32 Table 1.9: Probits Reporting Marginal Effects of ACT Percentile, Separated by Treatment 1st Stage, Any Round Any Stage, Any Round Dependent Variable: Cooperation in — Coefficient Std. Err. Coefficient Std. Err. NOSWITCH Top 5% 0.301** (0.131) 0.209** (0.095)

33 Result 5: Subjects with a score in the top 5% (below the top 20%) of all ACT test-takers are more (less) likely to cooperate than those with a score in the top 20% but below the top 5%.

For the NOSWITCH data, both regressions indicate that having a test score in the top 5% of all test-takers increases the likelihood of cooperation significantly compared to those with a score in the top 20% but not the top 5%, the baseline category. I also find that having a test score below the top 20% decreases the likelihood of cooperation compared to the baseline category in this treatment, although the effect is statistically significant only for the full NOSWITCH data set and not for first stage actions only. Hence, ACT scores provide evidence of a positive relationship between cognitive ability and cooperation in the standard prisoner’s dilemma environment. Because cooperative strategies are relatively complex in this environment and players with high cognitive ability should be more able to bear the cognitive costs of using complex strategies, this evidence is consistent with the idea that strategy choice is influenced by cognitive costs of strategic complexity. For all three of the other treatments, the estimated effect of having a score in the top 5% is positive in both regressions, but none is statistically significant. All but one of the corresponding estimates for having a score below the top 20% is negative (with the exception being for the full SWITCH-C data), and the estimate for first stage actions in NOSWITCH- R is statistically significant. Hence, it appears that the correlation between cognitive ability and cooperation remains but is attenuated in these treatments. Because a lower level of aggregate cooperation prevails in these treatments than in the baseline environment, a weaker correlation is not unexpected. It may be that the complexity of cooperative strategies in the baseline environment involves too high a cognitive cost for many subjects with low cognitive ability but not for those with high cognitive ability, but that the greater cognitive cost of using these strategies in the other treatments is prohibitive for many subjects with high cognitive ability as well. Table 1.10 reports the results of regressions on the pooled data from all four

34 treatments. In addition to the explanatory variables in the regressions reported in Table 1.9, the regressions on the pooled data include dummy variables to account for SWITCH-C, SWITCH-D and NOSWITCH-R treatment effects, interaction terms for phase II of each treatment, and terms controlling for interactions between the score percentile variables and all treatment and phase variables. This test reveals that the estimated relationship between ACT scores and cooperation does not differ significantly between the NOSWITCH baseline and the other treatments. The coefficient on the phase II dummy is positive and significant in both regressions for NOSWITCH-R, suggesting a general increase in cooperation due to learning over the course of this treatment. The same coefficient is positive but not statistically significant in all other regressions, suggesting that such learning is hampered by the additional cognitive cost of playing multiple simultaneous games in phase II of the other treatments. Interaction effects of ACT score and phase II display no consistent pattern and are statistically insignificant in all regressions except for first stage actions in NOSWITCH-R, where the effect of having a score below the top 20% in phase II is negative. This estimate indicates significantly less learning to cooperate over the course of a session among subjects with relatively low cognitive abiility. These results reveal evidence of a link between cooperation and cognitive ability as measured by ACT and SAT-ACT concordance scores. A correlation between average SAT scores in the subject pool and aggregate cooperation levels was previously reported by Jones (2008) in a metastudy of prisoner’s dilemma experiments. However, to my knowledge this study is the first to identify a link between cognitive ability and cooperation at the individual level. Because cooperative strategies are relatively complex and players with high cognitive ability should be more able to bear the cognitive costs of implementing complex strategies, this relationship supports the idea that strategy choice is influenced by cognitive costs of strategic complexity.

35 Table 1.10: Probits Reporting Marginal Effects of ACT Percentile, Treatment Interactions 1st Stage, Any Round Any Stage, Any Round Dependent Variable: Cooperation in — Coefficient Std. Err. Coefficient Std. Err. Top 5% 0.311** (0.134) 0.208** (0.095)

36 1.6 Conclusion

In this chapter, I study whether cooperation in the indefinitely repeated prisoner’s dilemma is sensitive to cognitive costs associated with strategic complexity. The complexity of strategies supporting cooperation in this game is increased through random switching between payoff tables during repeated games. Results indicate that increasing the complexity of cooperative strategies in this way reduces cooperation. The effect appears robust because cooperation is reduced regardless of whether the cooperate action or the defect action is manipulated to increase the complexity of cooperative strategies. The idea that cognitive costs of implementation complexity influence strategy choice is supported by a positive correlation between subjects’ ACT scores and cooperation, indicating that greater cognitive ability makes subjects more likely to use relatively complex strategies. To investigate possible interactions with the cognitive cost of strategic complexity, additional cognitive cost is introduced within this design through the play of multiple repeated games simultaneously. No evidence is found that the increased cognitive cost of playing multiple games reduces cooperation when multiple games are played after subjects have experience with isolated single games. However, comparison to a treatment in which subjects play multiple games before single games reveals that subjects cooperate less in the multiple game setting than in parallel single game rounds. This finding indicates that the additional cognitive cost of playing multiple games reduces subjects’ propensity to adopt a relatively complex cooperative strategy in each individual game. This experimental evidence may help to improve the applicability of game-theoretic predictions to real world problems. The results suggest that the cognitive cost of implementation complexity can influence strategy choice and ultimately the efficiency of outcomes, and they may be particularly relevant to some specific applications. Sustaining cooperation in the complex world in which we live often requires individuals to condition their actions not only

37 on the behavior of others, but also on the observable state of nature. The payoff table switching feature of this design simulates this source of complexity and shows that it can have an impact on cooperation. For example, consider collusion in a duopoly with a fluctuating but publicly observable demand state, where only the collusive price (if the competitive price is determined by a constant cost) or only the competitive price (if the collusive price is a constant “focal point” price) depends on demand fluctuations. Results of this experiment suggest that in either case, sustaining collusion is less likely than in an environment with relatively constant demand. The results regarding multiple games imply that cooperation among individuals is less likely if they are interacting with multiple opponents instead of only a single one, and that increasing the number of simultaneous interactions does not reduce cooperation among individuals who are experienced with their environment but may impair further development of cooperation. The results of this project suggest several possible lines of future experimental research. A similar design could be used to study the importance of strategic complexity in other common interest games such as public goods games or network formation games. The present work addresses the importance of implementation complexity in strategy choice, but the impact of limitations on a different but equally important type of complexity, computational complexity, also deserves investigation. Finally, the results found using data on subjects’ ACT scores highlight the value of collecting such data in experimental research and point to another line of future work exploring in more depth the link between cognitive ability and cooperation found in this study.

38 Chapter 2: An Experiment on Herding with Capacity Constraints

2.1 Introduction

In many choices between options of uncertain quality, individuals base their decisions on noisy private information about the quality of the options as well as what they can learn about quality from the observed choices of others. Such observational learning can lead to herding behavior, in which a sequence of individuals choose the same option having inferred from predecessors’ choices that the expected quality of that option is the highest. However, herding may be discouraged if costs are incurred when an individual follows the action of too many others. Observing other people on their way to one of several local restaurants or beaches, for example, provides information about the relative quality of their chosen option, but it also increases the likelihood that one who follows them to that option will incur a penalty because it has already reached capacity (e.g., the cost of waiting for a table or having insufficient space to sunbathe). A firm considering offering a new product may learn what types of products are in demand by observing the offerings of a rival, but if demand is already saturated then unanticipated, costly marketing measures may become necessary to make the venture profitable. An individual may copy the clothing style of a friend and, shortly after an expensive shopping trip, find that that style has gone out of fashion because too many people have adopted it. In these situations, a predecessor’s choice reveals information about the quality of the chosen option and the likelihood that its capacity has been reached, but

39 uncertainty about capacity remains because individuals do not observe the choices of all predecessors. Despite numerous applications, the importance of capacity constraints has so far received little attention in the literature on herding behavior.39 I attempt to address this issue by constructing a simple model of herding with imperfect information about predecessors’ choices similar to that of Celen and Kariv (2004b, 2005), with the addition of capacity constraints and a “waiting cost” incurred by individuals who choose an option after it has reached capacity. I then study behavior in this environment using a lab experiment in which subjects make choices in three different settings: (1) the standard Celen and Kariv setting with no capacity constraints, (2) the same setting with capacity constraints added and a low waiting cost predicted to attenuate but not dominate the incentive to herd, and (3) the setting with capacity constraints and a high waiting cost predicted to dominate the incentive to herd. Results of the experiment indicate that capacity constraints indeed discourage herding behavior, which highlights the importance of this consideration in many applications. I find that the capacity constraint and waiting cost have the predicted effects on the behavior of players earlier in the sequence of choices, whose tendency to follow their predecessors in the standard setting is reversed when capacity constraints are added. The magnitude of this effect depends as predicted on the size of the waiting cost. Similar results are found in some treatments for players later in the sequence, but because the problem of avoiding the waiting cost is more complex for these players their behavior is more heterogeneous. In addition to the practical insights gained from investigating behavior in a particular type of environment, this study provides a context for exploring broader questions about herding behavior. A common observation in herding experiments is that subjects rely more

39See Veeraraghavan and Debo (2008) and Eyster and Rabin (2010) for theory and Drehmann et al.(2007) and Owens (2011) for experiments on herding with negative externalities and perfect information about predecessors’ choices, a closely related environment.

40 on their private information and less on observational learning than predicted by theory.40 Two conjectures have emerged in the literature as the most plausible explanations for this consistent departure from equilibrium. It may be that individuals act rationally under the belief that predecessors sometimes err in making the rational choice, which justifies increased reliance on private information because what can be learned from others’ choices is less reliable. An alternative explanation is that individuals are boundedly rational in the sense that they fail to make inferences about unseen information from the choices they observe others make. Both of these departures from full, commonly known rationality would lead to over-reliance on private information, and the question of which is more influential lacks a definitive answer in the herding literature. The experimental design, which involves a sequence of four players choosing between options with a capacity of two, is equipped to provide evidence relevant to this discussion in several ways. Firstly, the choices of the first two players are made by computers whose decision rules are fixed and commonly known to human subjects taking the role of the third and fourth players. If over-reliance on private information is due to the chance that preceding human players make mistakes, replacing them with fully rational computers should eliminate this deviation from equilibrium. Secondly, if the waiting cost incurred when exceeding capacity is high, the fourth player’s choice is well-suited for comparison to fully rational and boundedly rational benchmarks. In the fully rational equilibrium of this setting the fourth player is predicted to follow the third unconditional on his private signal, but if the fourth player’s depth-of-reasoning is very limited he is predicted to choose contrary to the third player unconditional on his private signal. Thirdly, I include a treatment in which the second computer player’s choice reveals no information about the first computer player’s choice, which reduces the depth-of-reasoning involved in the fully rational strategies of the third and fourth players. Comparison of behavior in this environment to behavior in an

40See Celen and Kariv (2004a, 2005), Kubler and Weizsacker (2004), Goeree et al.(2007), Weizsacker (2010) and Ziegelmeyer et al.(2010).

41 environment where rational players make inferences about both the first and second players’ choices can provide insight into the importance of bounded rationality in herding behavior. Together, results of the experiment provide evidence that is more consistent with limited depth-of-reasoning than rationality with errors as an explanation for deviations from equilibrium. Despite knowledge that preceding players are fully rational computers, subject’s strategies in the setting with no capacity constraint do not differ markedly from those observed in other experiments in which all players are human. While none of the theoretical benchmarks considered provide a clearly superior fit with the data, the fourth player’s strategies are significantly closer to the fully rational equilibrium and significantly farther from boundedly rational benchmarks when the subject’s ACT or SAT-ACT concordance score is in the top 5% of all test-takers, an indicator of high cognitive ability. I also find that the behavior of the fourth player conforms more closely to the rational equilibrium in the treatment where rational strategies involve less depth-of-reasoning. These results suggest that limitations on players’ ability to make inferences from the choices of others plays an important role in herding behavior.

2.2 Related Literature

Studies of herding (see Banerjee 1992, Bikhchandani et al.1992, Smith and Sorensen 2000) have been concerned with determining when individuals choose contrary to their private information due to information learned from the observed actions of others. Experiments on herding commonly ﬁnd that subjects rely more on their private information and less on observational learning than predicted by the risk-neutral Bayes-Nash equilibrium.41 That subjects are less likely to follow the observed choices of others than predicted is particularly surprising because this tendency makes choices more revealing of private information than

41See Weizsacker (2010) for a review of these ﬁndings.

42 in equilibrium. This result emerges in both the standard binary-signal environment (see An- derson and Holt 1997, Anderson 2001) as well as a continuous-signal environment (see Celen and Kariv 2004a, 2005), where proximity to equilibrium behavior can be measured. Celen and Kariv (2005) find that subjects are even more likely to overweight private information when they observe only the choice of their immediate predecessor than when they observe the entire sequence of preceding choices. This setting with imperfect information about the choices of others is the baseline for the model presented in this study. A major discussion in the experimental herding literature has been whether deviations from equilibrium are best explained by rationality with errors, usually modeled as logistic or Quantal Response (see McKelvey and Palfrey 1995), or by bounded rationality, as in models of limited depth-of-reasoning such as Level-k thinking (see Stahl and Wilson 1994, Nagel 1995, Camerer et al.2004, and Crawford and Iriberri 2007) or Cursed Equilibrium (see Eyster and Rabin 2005). The evidence is mixed, with the best-fitting concept seemingly dependent on the context and modeling approach. Celen and Kariv (2004a, 2005) find that behavior fits a model of rationality with errors in the continuous-signal environment with perfect information. With imperfect information, they find to the contrary that a substantial proportion of players ignore their private information and rely too much on their predecessors’ actions.42 In longer sequences of observed choices, Goeree et al.(2007) find that herds are almost always disrupted by an individual with a disagreeing signal, which is consistent with Quantal Response. Results of an experiment on endogenous-timing investment by Ivanov et al.(2009) are not consistent with models of limited depth-of-reasoning, but they find that Quantal Response also produces an inferior fit compared to boundedly

42A similar rate of choices made unconditional on private information is found in this study.

43 rational rules-of-thumb. Ziegelmeyer et al (2010) study an experiment with low- and high- informed individuals and find that low-informed individuals behave consistently with Quan- tal Response, but high-informed individuals are more likely to follow others than predicted, contrary to the Quantal Response prediction. In contrast to studies which find at least some evidence in support of rationality with errors, a meta-study of 13 experiments by Weizsacker (2010) soundly rejects the hypothesis that the observed behavior is consistent with rational expectations. He finds that individuals rely too much on private information compared not only to the equilibrium but also compared to the empirically optimal choice. When private information contradicts the optimal choice given the true behavior of others, individuals in the experiments studied choose optimally 44% of the time, but when private information is consistent with the optimal choice, this frequency increases to 90%. This study indicates that herding behavior generally exhibits an overweighting of private information that is not explained by a rational response to the rate of errors by preceding players. Other studies find evidence that herding behavior is best explained by a combination of bounded rationality and response to error-rates. Kubler and Weizsacker (2004) conduct an experiment on herding with purchasing of costly signals, in which individuals choosing earlier in a sequence purchase too many signals, while later individuals purchase too few when the majority of predecessors chose the same action. They estimate a model which combines logistic response with limited depth-of-reasoning, allowing higher error rates on higher levels of reasoning, and find support for this model in their data. Brunner and Goeree (2011) also find support for such a model in an experiment where predecessors’ choices are observed but not the sequence in which they are made. They find evidence that the combination of Quantal Response and limited depth-of-reasoning explains individual behavior that is inconsistent with the predictions of these models taken individually.

44 Another possible explanation for the common deviation is that individuals are overconfi- dent in their private information, which causes them to discount information or advice given to them by others. Celen et al.(2010) address this issue using a design in which subjects receive advice on which option to choose from their immediate predecessor instead of or in addition to observing her actual choice. Surprisingly, advice leads to strategies that are closer to the equilibrium than choices made with observation alone, which indicates that advice discounting is not to blame for over-reliance on private information. Other experiments have studied herding behavior in environments where individuals receive direct payoff externalities in addition to information externalities from the choices of others. An experiment by Hung and Plott (2001) includes a treatment in which players are rewarded for choosing the same option as the majority, and subjects are found to rely less on their private information and follow predecessors more often in this treatment than in the standard Anderson and Holt (1997) environment. An internet experiment by Drehmann et al.(2007) adds positive and negative payoff externalities to the standard environment so that individuals receive a bonus or penalty for each player who chooses the same as they do. This study also finds that subjects are less reliant on private signals and more responsive to the choices of others when such payoff externalities are present.43 Though the results of the above experiments on herding with payoff externalities are intuitive, they lack a solid theoretical benchmark for comparison. In contrast, Owens (2011) provides theoretical benchmarks for his experiment on herding in simple two-player sequences with both positive and negative payoff externalities. Consistent with previous literature, he finds that second-movers are less responsive to information externalities than predicted in the RNBNE, but he also finds that they are more responsive to payoff externalities than

43Another interesting result of the Drehmann et al.(2007) study is that their subjects behave myopically, acting as though only predecessors’ choices matter when the choices of followers also affect payoffs. The model used in this study assumes that the choices of followers do not affect payoffs, but this experimental evidence suggests that behavior may not differ substantially if this assumption were relaxed.

45 predicted. Owens shows that neither risk-aversion nor Quantal Response explain these results well. An additional treatment in which first-movers are perfectly rational computers provides evidence that ambiguity about the rationality of first-movers partially explains deviations from equilibrium by second-movers in other treatments. However, he does not explore bounded rationality as an alternative explanation for the experimental results. Aside from the model of Owens (2011), the theory most closely related to the model in this paper is a study in the management/operations research literature by Veeraraghavan and Debo (2008). They develop a model of rational consumers choosing between two queues leading to services of uncertain quality after receiving a private signal about the quality and learning the length of the queues. As in this study, they investigate the tradeoff between the incentives to maximize expected quality by following the crowd and to avoid the cost of waiting in the longer queue. They find that herding is discouraged when the cost of waiting is high, as I do in my model, and they explore the implications of this result for strategic location of services. Eyster and Rabin (2010) discuss a variant of their model of naive herding which considers the consequences of a small negative externality of choosing the same as others, with negative consequences for efficiency.

2.3 Model

I consider a model of herding with continuous signals,44 imperfect information about predecessors’ actions45 and capacity constraints. Four players, indexed by n ∈ {1, 2, 3, 4}, choose between options R and L in sequence. The choice of player n is denoted by xn. Before

choosing, each player observes xn−1 and receives a private signal about option quality, θn, drawn independently and uniformly from the interval [0, 1]. The quality of option R is equal P4 P4 i=1 θi i=1 θi to 4 , while the quality of option L is equal to 1 − 4 . Each option has a capacity

44See Smith and Sorensen (2000), Celen and Kariv (2004a, 2004b, 2005) and Owens (2011) 45See Celen and Kariv (2004b, 2005).

46 of two. Player n’s payoﬀ from choosing an option is equal to the quality of the option minus

that player’s waiting cost, Cn(x1, ..., xn), which is equal to c ∈ [0, 1] if at least two of n’s predecessors chose the same option as n and 0 otherwise.

Suppose xn−1 = R. Player n chooses option R if and only if the following holds:

P4 i=1 θi E[U( 4 − Cn(x1, ..., xn−1,R))|θn, xn−1 = R] P4 i=1 θi ≥ E[U(1 − 4 − Cn(x1, ..., xn−1,L))|θn, xn−1 = R].

By monotonicity of U in θn, it follows that player n uses a decision rule given by:

  ˆ R if θn ≥ θn xn(xn−1 = R) = .  ˆ L if θn < θn

The problem is symmetric for xn−1 = L, so in this case player n follows a decision rule given by:   ˆ R if θn ≥ 1 − θn xn(xn−1 = L) = .  ˆ L if θn < 1 − θn

ˆ Therefore, the equilibrium is fully characterized by θn as a function of c for each n. I refer ˆ to θn as player n’s equilibrium strategy at waiting cost c.

47 2.3.1 Risk-Neutral Bayesian Nash Equilibrium

ˆ The Risk-Neutral Bayesian Nash Equilibrium (RNBNE) strategies, θn, for the four players are:

   1 (39 + 368c − 576c2) if c ≤ 13  256 24  3+24c if c ≤ 13  ˆ 1 ˆ 1 ˆ  16 24 ˆ  θ1 = , θ2 = , θ3 = , θ4 = 13−16c if c ∈ ( 13 , 13 ] . 2 4 16 24 16 1 if c > 13   24   13 0 if c > 16

Derivation of the RNBNE is relegated to Appendix B.46 The RNBNE strategies for Players ˆ ˆ 3 and 4 (P3 and P4), θ3 and θ4, are shown as a function of the waiting cost, c, in Figure 2.1.

5 For low waiting costs (c < 24 ), the incentive to choose the option with the highest quality dominates, and the usual herding results apply. Player 3 (P3) follows Player 2 (P2) when

her private signal agrees with P2’s choice (θ3 ≥ 50 if x2 = R and θ3 ≤ 50 if x2 = L) or when it disagrees weakly. However, the range of disagreeing signals for which P3 follows

5 13 P2 shrinks as the waiting cost increases. For moderate costs (c ∈ [ 24 , 24 )), the incentive to avoid the cost causes P3 to choose contrary to P2 for all disagreeing private signals as well as weak agreeing signals, and the range of agreeing signals for which P3 follows P2 shrinks

13 as the cost increases. When the waiting cost is suﬃciently large (c ≥ 24 ), the incentive to avoid the cost dominates the incentive to choose the highest-quality option, so P3 chooses contrary to P2 unconditional on her private signal. For low costs, results for Player 4 (P4) are similar to those for P3 except that the informational externality of P3’s choice is slightly larger than that of P2’s, so P4 follows P3

46In Appendix B, I explore the impact of risk-aversion on the Bayesian Nash Equilibrium. I ﬁnd numerical solutions for the equilibrium strategies of P3 and P4 under rather extreme risk-aversion, which bear negligible diﬀerences from the RNBNE strategies with one exception. The equilibrium strategy for a risk-averse P4 with c = .85 chooses contrary to P3 for a substantial range of strong disagreeing signals, whereas the RNBNE strategy is to follow P3 unconditional on his private signal. Hence, if risk-aversion plays an important role in the experiment, it should express itself in deviations from the RNBNE only for P4 at a high waiting cost level.

48 Figure 2.1: RNBNE Strategies for Players 3 and 4

for a slightly larger range of disagreeing private signals. When the cost is low, the range of disagreeing signals for which P4 follows P3 shrinks as the cost increases. However, because increasing the cost raises the likelihood that P3 chooses contrary to P2, and because P2 follows Player 1 (P1) with probability 3/4, increasing the cost raises the likelihood that P4 can avoid the cost by following P3. At the same time, increasing the cost makes avoiding it more important, so the range of signals for which P4 follows P3 begins to increase with

23 the cost when it reaches c = 72 . The range of signals for which P4 follows P3 continues to 13 increase with the cost until it reaches c ≥ 16 , where the incentive to avoid the cost dominates and P4 follows P3 unconditional on his private signal.

49 2.3.2 Bounded Rationality

I now consider how P3 and P4 behavior may diﬀer from the RNBNE if they fail to make inferences about expected option quality based on the observed choices and rationality of others. The Level-k model originated by Nagel (1995) and Stahl and Wilson (1994) and extended to Bayesian games by Camerer et al (2004) and Crawford and Iriberri (2007) provides benchmarks which represent such limitations on depth-of-reasoning in this environment. In the Level-k model, a Level-0 player is assumed to choose an option randomly, a Level-1 player best-responds to the belief that others are Level-0, a Level-2 player best-responds to the belief that others are Level-1, and a Level-k player best-responds to the belief that others are Level-k − 1. The Level-1 equilibrium concept closely resembles the Cursed Equilibrium of Eyster and Rabin (2005), and in fact the Level-1 and Cursed Equilibrium strategies are identical in this model.47 Similarly, the Level-2 equilibrium of this model is identical to the Best Response Trailing Naive Inference Equilibrium of Eyster and Rabin (2010). Because P1 and P2 are computers whose choice rules are ﬁxed and known to all human players in this experiment, incorrect beliefs about the rationality of these players on the part of P3 seems rather implausible. However, limitations on depth-of-reasoning may cause subjects in the experiment to behave as if they hold incorrect beliefs about P1 and P2’s behavior.48 The Level-k strategies of Players 3 and 4 are shown in Figures 2.2 and 2.3. Player 3’s Level-k strategy coincides with the RNBNE for Level-3 and higher. Player 4’s Level-k strategy coincides with the RNBNE for Level-4 and higher, and his Level-3 strategy is very close to his RNBNE strategy. Hence, I focus on the Level-1 and Level-2 strategies as the

47As discussed in Eyster and Rabin (2009), Cursed Equilibrium and Level-1 predictions coincide in most cases, including this one, but Level-1 players believe that others’ choices are uniformly distributed while Cursed players’ beliefs about the distribution of others’ choices are not necessarily uniform. 48See Charness and Levin (2009) for an experiment on one-person decision problems where such boundedly rational play persists absent beliefs about the rationality of others.

50 Figure 2.2: Level-k Strategies of Player 3

interesting benchmarks of boundedly rational behavior in this environment. These Level-k strategies are derived in Appendix B. A Level-1 player n observes her own private signal and player n − 1’s choice but believes that it reveals nothing about n − 1’s private signal or player n − 2’s choice. Hence, with no capacity constraint she simply follows her private information, and with a capacity constraint she has an incentive to choose contrary to her immediate predecessor to reduce the chance of incurring the waiting cost. Because choosing contrary to her immediate predecessor reduces the chance of incurring the cost by 50 percentage points according to the beliefs of both the Level-1 P3 and the Level-1 P4 (50% to 0% for P3 and 75% to 25% for P4), the Level-1 strategies are the same for both P3 and P4. These Level-1 strategies diﬀer in an important way from the RNBNE strategies. For low waiting costs, a Level-1 P3 or P4 chooses contrary to her immediate predecessor for all disagreeing and weak agreeing signals, which eliminates

51 Figure 2.3: Level-k Strategies of Player 4

herding. When the cost is high, a Level-1 P3 or P4 chooses contrary to her immediate predecessor unconditional on her private signal. While this strategy coincides with the RNBNE strategy for P3 at high costs, it is the opposite of the RNBNE strategy for P4, which follows P3 unconditional on her private signal at high costs. A Level-2 player n accounts for the fact that player n − 1 chooses based on her own

private signal (θn−1) and the observed choice of player n − 2 (xn−2) but believes that player n − 1 does not make inferences from player n − 2’s choice about preceding private signals

(θn−2, θn−3, ...) or choices (xn−3, xn−4, ...). Because the Level-2 P3 fails to learn about P1’s choice from P2’s observed choice, her strategy places more weight on her private signal than the RNBNE strategy for all but very high waiting costs, where they coincide. For the same reason, P4’s Level-2 strategy involves less-than-rational observational learning (i.e., the range of disagreeing signals for which P4 follows P3 is smaller than in the RNBNE) with small

52 waiting costs. When the cost is large, a Level-2 P4 recognizes that P3 chooses opposite of P2 but does not recognize that P2 is expected to follow P1. Instead, P4 believes that following P3 makes incurring the cost and not incurring the cost equally likely. P4 thus conditions his choice at high costs on his private signal, choosing contrary to P3 given a disagreeing or weak agreeing private signal and following P3 given a strong agreeing signal. Hence, for high costs P4’s Level-2 strategy is conditional on the private signal while his RNBNE and Level-1 strategies are not.

2.4 Experimental Design

Each session of the experiment consists of 18 rounds. In each round, subjects are matched randomly and anonymously in pairs: one subject with the role of P3 and the other, P4. P3 and P4 roles are assigned randomly to subjects at the beginning of the experiment, and subjects keep the same role throughout. In each round, P3 and P4 make a choice after choices are made by two computer players, P1 and P2. P1 and P2 are computers because the main contribution of this study is in the insight gained from the behavior of P3 and P4, but their behavior is most interesting when P1 and P2 choose rationally, providing an informational externality through their choices. Each round has exactly the same rules as the game presented in Section 2.3, except that the private signals and waiting cost are multiplied by 100. Each player chooses one of two options, RIGHT (R) and LEFT (L), in sequence. Before choosing, subjects see only the waiting cost for that round and the choice of the immediately preceding player on their computer screens. The experiment uses a belief elicitiation procedure for entering choices,49 by which subjects are asked to enter a number between 0 and 100 before their private signal is shown to them. If the private signal turns out to be greater than this number, the subject’s

49This method has been used in previous continuous-signal herding experiments by Celen and Kariv (2004a, 2005), Celen et al. (2010) and Owens (2011).

53 Figure 2.4: Computer Player Strategies

MIXED and ORDERED NAIVE-MIXED

choice is R, and if the private signal turns out to be less than this number, the subject’s choice is L. After a number is entered, the private signal is drawn and shown on the subject’s computer screen along with the resulting choice, the payoﬀ associated with this choice, the cost incurred (if any) and net earnings for the round. The experiment includes three treatments: MIXED, ORDERED and NAIVE-MIXED. In each treatment, the strategies followed by computer players P1 and P2 are shown to subjects on a diagram. Figure 2.4 reproduces the diagrams shown to subjects in each of the three treatments.50 In MIXED and ORDERED, P1 and P2 choose according to the RNBNE strategy. In NAIVE-MIXED, P2 chooses naively in that it ignores the choice of P1 and makes its choice ˜ based entirely on its private signal (θ2 = 50 unconditional on x1). Therefore, the RNBNE for P3 and P4 involves less depth-of-reasoning in this treatment, as P3’s RNBNE strategy coincides with her Level-2 strategy and P4’s strategy coincides with his Level-3 strategy.

50See Appendix B for the instructions given to subjects and screenshots of the choice and feedback screens. The experimental software is programmed in zTree (Fischbacher, 2007).

54 Figure 2.5: Player 4 Strategies in NAIVE-MIXED

P3’s Level-k strategies in NAIVE-MIXED are the same as in the other treatments, but P4’s Level-3 strategy is different because it best-responds to a Level-2 P2, and in NAIVE-MIXED P2’s Level-2 and Level-1 strategies are identical whereas in the other treatments they differ. P4’s Level-k and RNBNE strategies in NAIVE-MIXED are derived in Appendix B and shown in Figure 2.5. In each round, the waiting cost is set at one of three values: 0, 35 or 85. I refer to 0-cost rounds as the No-Cap setting, 35-cost rounds as the Low-Cost setting, and 85-cost rounds as the High-Cost setting. In all three treatments, six of the 18 rounds in the experiment are played at each cost level. In MIXED and NAIVE-MIXED, the order in which these rounds are played is determined randomly. In ORDERED, the No-Cap rounds are played first,

55 followed by the Low-Cost rounds and lastly the High-Cost rounds.51 Payoﬀs are denominated in Experimental Currency Units (ECUs). Subjects receive a starting balance of 50 ECUs plus their earnings in one randomly determined round out of the six played at each cost level (three rounds total). They are paid cash at an exchange rate of $0.10 per ECU, in addition to a ﬁxed participation fee of $5.

2.5 Experimental Questions and Results

Sessions were conducted at the Ohio State University Experimental Economics Lab in the fall of 2011. A total of 166 subjects participated in the experiment with 60 participating in MIXED over 3 sessions, 56 participating in ORDERED over 2 sessions, and 50 participating in NAIVE-MIXED over 2 sessions. All subjects participated in one and only one of the three treatments, so all treatment differences are between-subject, while differences across No-Cap, Low-Cost and High-Cost settings in each treatment are within-subject. Subjects were recruited via email invitations sent out randomly to students in a large database of Ohio State undergraduates of all majors. Sessions lasted between 60 and 90 minutes, with average earnings of $22.15. The advantage of the strategy-elicitation method used in the experiment is that it allows me to determine proximity to equilibrium behavior and to infer the degree to which strategies rely on private information vs. observational learning. In this section, I analyze all of the strategies entered by subjects as if the immediately preceding player chose R. Figure 2.6 displays the distributions of strategies entered by subjects in each treatment split by cost level and the choice of the immediately preceding player (R or L). These figures show that the distribution of strategies when the preceding player chose R and the distribution when the preceding player chose L are reasonably symmetric, with no consistent bias towards R

51Two trial rounds which do not count for payment precede these 18 rounds so that subjects can become familiar with the software interface. In MIXED and NAIVE-MIXED, the cost level in trial rounds is drawn randomly and independently from {0, 35, 85}. In ORDERED, the cost level is 0 in both trial rounds.

56 Figure 2.6: Distribution of Strategies by Treatment/Setting/Preceding Player Choice

Player 3

Player 4

57 or L.52 Hence, I simplify the analysis henceforth by collapsing the data into one dimension of strategies which combines the strategies entered when the preceding player chose R with 100 minus the strategies entered when the preceding player chose L.

Question 1: Compared to previous studies with human preceding players, in which strategies tend to overweight private information, do strategies exhibit more observational learning when predecessors are fully rational computers?

An important diﬀerence between this experiment and other herding experiments is that instead of making a choice given information the behavior of other humans, P3’s predecessors are computer players whose strategies are commonly known and (in MIXED and ORDERED) fully rational. This feature of the design allows me to test the hypothesis that players in other studies are over-reliant on private information due to the possibility that preceding human players make mistakes. To address this issue, I compare P3 and P4 strategies in my experiment to those of Celen and Kariv’s (2005) experiment, in which the environment for P3 and P4 is equivalent to the No-Cap setting of MIXED and ORDERED except that the preceding players are human subjects instead of computers.

Question 2: How does the capacity constraint aﬀect the strategies of Players 3 and 4?

The theoretical model predicts that a capacity constraint can either attenuate or reinforce herding depending on the player, treatment and setting. In all three treatments, the capacity constraint is predicted to shift P3 strategies such that following P2 is less likely. While P3

52Kolmogorov-Smirnov tests find no significant differences in the distribution of strategies when the preceding player chose R and the mirror image of the distribution when the preceding player chose L in any treatment/setting combination, except at the .1 level for P3 in No-Cap rounds of ORDERED and NAIVE- MIXED and for P4 in High-Cost rounds of NAIVE-MIXED, where the difference is accounted for by a few subjects who always enter a strategy of 100 in these settings.

58 is predicted to follow P2 for all agreeing private signals and for weak disagreeing signals in No-Cap rounds, she is predicted to choose contrary to P2 for all disagreeing and weak agreeing signals in Low-Cost rounds. In High-Cost rounds, the incentive to avoid the waiting cost dominates, so P3 is predicted to choose contrary to P2 unconditional on her private signal. For P4, the waiting cost is predicted to have a non-monotonic eﬀect on strategies in MIXED and ORDERED. He is predicted to follow P3 for all agreeing signals and weak disagreeing signals in both No-Cap and Low-Cost rounds, but the range of disagreeing signals for which P4 follows P3 is smaller in Low-Cost than in No-Cap rounds. In High-Cost rounds, however, the incentive to avoid the waiting cost dominates, so P4 is predicted to follow P3 unconditional on his private signal in MIXED/ORDERED, while he is predicted to choose contrary to P3 for all disagreeing and weak agreeing private signals in NAIVE-MIXED.

Question 3: How do the strategies of Players 3 and 4 diﬀer when Player 2’s strategy is unconditional on Player 1’s choice, compared to when Player 2’s strategy is rational?

I am also interested in testing for differences in behavior between treatments. Because the underlying game is identical in both MIXED and ORDERED, I should observe no difference between these two treatments for either P3 or P4 unless the order in which settings are played affects behavior in some way. However, differences between NAIVE-MIXED and MIXED/ORDERED should shed light on how depth of reasoning by P3 and P4 compares to theoretical predictions. In NAIVE-MIXED, the RNBNE strategies for P3 and P4 are identical to their Level-2 and Level-3 strategies, respectively, while in MIXED/ORDERED, the RNBNE strategies require deeper reasoning (Level-3 and Level-4). In NAIVE-MIXED, P3’s RNBNE strategy involves less observational learning than in MIXED/ORDERED because no information about P1’s

59 Table 2.1: Summary of Strategies by Treatment and Setting No-Cap Low-Cost High-Cost Treatment Mean =0 =100 Mean =0 =100 Mean =0 =100 Player 3 MIXED 45.2 16.1% 10.6% 66.4 2.8% 21.1% 70.5 2.2% 30.6% ORDERED 50.4 11.9% 8.3% 59.6 8.3% 16.1% 76.3 2.4% 38.1% NAIVE-MIXED 42.3 20.7% 8.0% 69.3 3.3% 25.3% 77.8 1.3% 36.0% Player 4 MIXED 52.2 15.0% 13.9% 49.6 18.9% 12.2% 45.9 17.2% 14.4% ORDERED 43.8 9.5% 4.2% 52.4 10.7% 10.1% 52.3 14.9% 14.3% NAIVE-MIXED 51.0 8.0% 10.7% 57.8 5.3% 6.0% 62.6 6.0% 10.0%

choice can be inferred from the observed choice of P2. However, the important diﬀerence between treatments is in P4’s RNBNE High-Cost strategies. In MIXED/ORDERED, P4’s RNBNE High-Cost strategy is to follow P3 unconditional on his private signal, whereas in NAIVE-MIXED, it is to follow P3 for strong agreeing signals only and choose contrary to P3 for all disagreeing and weak agreeing signals. For each treatment and setting, Table 2.1 summarizes strategies entered by P3 and P4 (with strategies entered when the preceding player chose L transposed as if she had chosen R) along with the percentage of strategies which unconditionally follow (a strategy of 0) or unconditionally choose contrary to (a strategy of 100) the immediately preceding player. Figure 2.7 displays the distribution of strategies in each treatment and setting for P3 and P4 with the RNBNE prediction marked by a vertical line.

Result 1: In rounds with no capacity constraint, mean strategies of both Players 3 and 4 suggest that they rely more on the private signal and less on observational learning than predicted. However, a substantial proportion of strategies involve more observational learning

60 Figure 2.7: Distribution of Strategies by Treatment and Setting

Player 3 Player 4

than predicted, with choices made unconditional on the private signal.

The mean No-Cap strategies are similar to those reported by Celen and Kariv (2005), which are equivalent to 45 for P3 and 44 for P4 in terms of my parameters. Mean strategies in both experiments exhibit over-reliance on private information. Indeed, Wilcoxon signed- ranks tests show that none of the mean No-Cap strategies are signiﬁcantly less than 50 at the .1 level., where 50 is the strategy which relies entirely on the private signal with no observational learning.53 However, a relatively high proportion of No-Cap strategies in MIXED and NAIVE-MIXED are unconditional on the private signal.54 These strategies thus exhibit much more observational learning than predicted, which contrasts with the

53Because the Bayesian Nash Equilibrium with risk-aversion predicts a substantial deviation from the RNBNE only in High-Cost rounds of MIXED and ORDERED, that there is a substantial deviation in all rounds suggests that risk-aversion does not explain deviations from equilibrium. 54For comparison, Celen and Kariv report a 17.5% rate of such strategies in their experiment.

61 overweighting of private information suggested by the mean strategies in this and other experiments.55 Hence, it appears that mean strategies do not tell the whole story, and that the distribution of strategies must be studied in more detail.56 Compared to MIXED and NAIVE-MIXED, P3 and P4 strategies are distributed closer to 50 in the No-Cap and Low-Cost settings of ORDERED, which is identical to MIXED except that No-Cap rounds are played first, then the Low-Cost rounds, and finally the High-Cost rounds. In other words, when the equilibrium is in the interior of the interval, strategies are distributed more in the interior when these rounds are played before any rounds in which the equilibrium is at an endpoint (ORDERED) than when they are played in a random sequence with such rounds (MIXED). This difference suggests that behavior when the sequence of settings is random is subject to considerable hysteresis across settings. In rounds where the equilibrium is at an endpoint of the interval, a high proportion of P3 strategies are at the same endpoint, while P4 strategies are distributed roughly equally at that endpoint and the opposite endpoint. Hence, P4 behavior is quite heterogeneous in rounds where the RNBNE is to follow P3 unconditional on the private signal, with many subjects doing the opposite.

2.5.1 Eﬀects of the Capacity Constraint

Table 2.2 reports the mean strategies entered by P3 and P4 in each treatment and setting along with the RNBNE prediction. I use a Wilcoxon signed-ranks test to determine whether the capacity constraint and waiting cost have the predicted within-subject eﬀects on strategies, and I use a Wilcoxon rank-sum test to determine whether there is any signiﬁcant

55See the results of Celen and Kariv (2004, 2005) for direct comparisons or the survey of Weizsacker (2010) for more general ﬁndings. 56This ﬁnding raises an important methodological issue in analyzing experiments of this type.

62 Table 2.2: Predicted vs. Actual Eﬀects of Treatment and Setting on Strategies RNBNE Mean Strategies Treatment No-Cap Low-Cost High-Cost No-Cap Low-Cost High-Cost Player 3

MIXED 18.8 71.3 100.0 45.2 <<< 66.4 70.5

ORDERED 18.8 71.3 100.0 50.4 < 59.6 <<< 76.3

NAIVE-MIXED 25.0 60.0 100.0 42.3 <<< 69.3 << 77.8 Player 4 MIXED 15.2 38.0 0.0 52.2 49.6 45.9

ORDERED 15.2 38.0 0.0 43.8 < 52.4 52.3 NAIVE-MIXED 18.8 59.0 75.0 51.0 57.8 62.6**

Difference between settings significant at: <<<.01 level, <<.05 level, <.1 level. Difference from MIXED treatment significant at: *** .01 level, ** .05 level, * .1 level.

between-subject diﬀerence in strategies across treatments.57

Result 2.1: Player 3 strategies are such that following Player 2 is (a) less likely in rounds with a capacity constraint than without and (b) less likely in rounds with a high waiting cost than a low waiting cost.

P3 strategies exhibit the predicted comparative static effects of the capacity constraint and waiting cost, i.e., increasing the cost from 0 to 35 and from 35 to 85 shifts P3 strategies such that choosing contrary to P2 to avoid the cost is more likely. P3’s Low-Cost strategies make following P2 significantly less likely than her No-Cap strategies in all three treatments, and her High-Cost strategies make following P2 significantly less likely than her Low-Cost

57Treatment differences are also analyzed using random effects GLS regressions. Every treatment difference that is significant according to the Wilcoxon tests is significant according to the regressions and vice versa, but the level of significance according to the Wilcoxon tests is sometimes weaker.

63 strategies in ORDERED and NAIVE-MIXED, but the eﬀect is not signiﬁcant in MIXED.58

Result 2.2: When all rounds without a capacity constraint are played before rounds with a capacity constraint, Player 4 strategies are such that following Player 3 is less likely in rounds with a capacity constraint than without.

The only case in which the capacity constraint has a significant effect on P4 strategies is in ORDERED, where his Low-Cost strategies make him significantly less likely to follow P3 than his No-Cap strategies, as predicted. That the effect is significant in ORDERED but not the other treatments is surprising because the predicted effect is larger in NAIVE-MIXED than in the other two treatments, so the effect should be significant in this treatment if no other. This result is consistent with the idea that hysteresis of strategies between settings causes a dampening of their effects in MIXED and NAIVE-MIXED, where the sequence of settings is random.

Result 3.1: No evidence is found that Player 3 strategies exhibit more observational learning when Player 2 choices are conditional on Player 1 choices, compared to when they are not.

I find no significant difference in P3 strategies between treatments. However, it is interesting to note that P3’s Low-Cost stategies in NAIVE-MIXED are the only case for either Player in which the mean strategy is farther from 50 than predicted, indicating an under- reliance on private information.

58It is important to note that substantial losses are possible in High-Cost rounds if players incur the cost, which means that loss aversion could create a potential confound with a rational response to the cost in this setting. Alevy et al.(2007) find experimental evidence that herding behavior can be influenced by loss aversion. However, that the response to the cost in the Low-Cost setting is as predicted by comparitive statics in the RNBNE suggests that differences in strategies across settings are not explained by loss aversion because substantial losses in the Low-Cost setting are extremely unlikely.

64 Table 2.3: Mean Strategies, First Round and Last Round in Each Setting Player 3 Player 4 Treatment Setting RNBNE First Last RNBNE First Last MIXED No-Cap 18.8 50.4 39.8 15.2 60.8 46.0 Low-Cost 71.3 64.2 71.3 38.7 56.1 45.5 High-Cost 100.0 56.9 78.0 0.0 48.6 40.1 ORDERED No-Cap 18.8 54.6 45.6 15.2 44.3 46.5 Low-Cost 71.3 61.1 56.5 38.7 40.4 63.1 High-Cost 100.0 67.1 82.1 0.0 63.9 47.5 NAIVE-MIXED No-Cap 25.0 48.8 50.1 18.8 53.8 55.2 Low-Cost 60.0 61.8 78.0 59.0 56.5 60.5 High-Cost 100.0 73.2 78.7 75.0 60.8 66.3

Result 3.2: When the High-Cost RNBNE is for Player 4 to choose contrary to Player 3 for all disagreeing and weak agreeing private signals, Player 4’s strategies diﬀer as predicted from her strategies when the High-Cost RNBNE is to follow Player 3 for all private signals.

As for treatment effects, the only significant difference is between P4’s High-Cost strategies in MIXED and NAIVE-MIXED. Compared to MIXED, P4 strategies in NAIVE-MIXED shift significantly towards choosing contrary to P3, which is consistent with the most extreme treatment effect predicted in this experiment. This result suggests that P4 strategies incor- porate some depth-of-reasoning in attempting to avoid the waiting cost. Although mean P4 strategies do not display the non-monotonic pattern across cost levels predicted by the RNBNE in MIXED and ORDERED, when I restrict my attention to only P4 strategies entered in the last round in each setting in MIXED, a non-monotonic pattern is evident. Table 2.3 reports the mean strategies in subjects’ first and last of the six rounds played in each setting in each treatment for both P3 and P4. Mean strategies entered by both P3 and P4 in MIXED show a consistent shift towards the RNBNE between the first and last round played

65 in each setting, which indicates learning in the direction of the RNBNE in this treatment. However, the data from the other two treatments do not show a similar tendency.

2.5.2 Subjects Satisfying Basic Rationality

The distributions of strategies in Figure 2.7 reveals that subjects’ strategies vary widely in some settings and treatments, particularly for P4, whose behavior is quite heterogeneous. A substantial proportion of subjects in both roles use No-Cap strategies which are not even minimally consistent with the RNBNE, choosing contrary to their immediate predecessor given an agreeing signal even though there is no rational reason to do so. In order to reduce noise created by the strategies of these subjects, I now restrict my attention to only those subjects whose mean No-Cap strategies satisfy basic rationality in that they do not choose contrary to their immediate predecessor given an agreeing signal, i.e., their mean No-Cap strategy is less than or equal to 50 (hereafter called BR subjects). The percentages of BR subjects are 56.7%, 46.4% and 56.0% for P3 and 43.3%, 67.9% and 56.0% for P4 in MIXED, ORDERED and NAIVE-MIXED, respectively.59 The distributions of BR subjects’ strategies across treatments and cost levels are presented Figure 2.8. Table 2.4 reports the mean strategies of BR subjects by treatment and setting along with the RNBNE predictions and results of the same Wilcoxon tests performed on the full data.60

Result 3.3: Among subjects satisfying basic rationality, the eﬀects of the capacity constraint, waiting cost and treatment on Player 4 strategies are as predicted when the RNBNE strategy

59For comparison, Celen and Kariv (2005) report that 60.8% of strategies in their experiment satisfy the basic rationality condition. 60Treatment differences for BR subjects are also analyzed using random effects GLS regressions. Results of the Wilcoxon tests are more conservative in that every treatment difference that is significant according to the Wilcoxon tests is significant according to the regressions and vice versa, but the level of significance according to the Wilcoxon tests is sometimes weaker.

66 Figure 2.8: Distribution of BR Subjects’ Strategies by Treatment and Setting

Player 3 Player 4

coincides with the Level-3 strategy.

Although they are larger and more statistically significant among BR subjects, differences in P3 strategies between settings are not qualitatively different from the results obtained from the full data. For P4, however, Low-Cost strategies differ significantly from No-Cap strategies as predicted in NAIVE-MIXED as well as ORDERED, although the effect remains insignificant in MIXED. I also find that P4’s High-Cost and Low-Cost strategies differ significantly as predicted in NAIVE-MIXED among BR subjects. Hence, the capacity constraint and waiting cost effects among BR subjects with the role of P4 are consistent with the RNBNE if it coincides with the Level-3 strategy. In the other two treatments, where the RNBNE involves deeper reasoning than Level-3 (Level-4), the strategies of BR subjects in the P4 role do not display the predicted differences across settings. Differences in P4’s Low- and

67 Table 2.4: Eﬀects of Treatment/Setting on Strategies of Subjects Satisfying Basic Rationality

RNBNE Mean Strategies Treatment No-Cap Low-Cost High-Cost No-Cap Low-Cost High-Cost Player 3

MIXED 18.8 71.3 100.0 26.9 <<< 63.6 70.4

ORDERED 18.8 71.3 100.0 37.6* << 56.6 <<< 82.9

NAIVE-MIXED 25.0 60.0 100.0 27.0 <<< 73.4 <<< 84.1 Player 4 MIXED 15.2 38.0 0.0 32.9 29.6 33.0

ORDERED 15.2 38.0 0.0 33.0 << 50.0** 50.5

NAIVE-MIXED 18.8 59.0 75.0 41.8* << 53.8** << 64.7***

Difference between settings significant at: <<<.01 level, <<.05 level, <.1 level. Difference from MIXED treatment significant at: *** .01 level, ** .05 level, * .1 level.

High-Cost strategies between NAIVE-MIXED and MIXED treatments are also statistically significant among BR subjects such that following P3 is less likely in NAIVE-MIXED, as predicted. This finding suggests that subjects who satisfy a basic rationality benchmark in rounds with no capactiy constraint conform reasonably well to the RNBNE in rounds with a capacity constraint when it requires reasoning no deeper than Level-3. Although theoretical predictions are identical in MIXED and ORDERED, it appears that playing No-Cap rounds before rounds with a capacity constraint induces different behavior from when settings are played in a random sequence. Among BR subjects, P3’s No-Cap strategies and P4’s Low-Cost strategies are significantly closer to 50 in ORDERED than in MIXED. This difference is seemingly due to hysteresis of strategies across settings in MIXED, where settings are played in a random sequence. Here, the tendency to make choices unconditional on the private signal in High-Cost rounds, where such strategies are the equilibrium, spills over to strategies in Low-Cost and No-Cap rounds, where the equilibrium strategy conditions choices on the private signal.

68 Table 2.5: Cost Level in Trial Rounds and Rounds 1-6 of MIXED/ORDERED

Treatment Session T1 T2 1 2 3 4 5 6 MIXED 1 0 35 35 85 0 85 0 85 MIXED 2 85 35 0 0 35 35 0 35 MIXED 3 35 35 85 35 0 85 85 85 ORDERED Pooled 0 0 0 0 0 0 0 0

Support for this interpretation is found in a relationship between the frequency of choices made unconditional on the private signal (corner strategies) and how the random sequence of settings differs between individual sessions of MIXED. Table 2.5 lists the sequence of cost levels in the two trial rounds and the first six paid rounds in the three MIXED sessions. All of these rounds were No-Cap in ORDERED. The distributions of strategies in No-Cap rounds within the first 6 paid rounds of MIXED sessions are shown in Figure 2.9. P3 distributions show a disproportionate amount of corner strategies in Session 3, where only one of the first six paid rounds and neither trial round is No-Cap. In Sessions 1 and 2, however, 3 of these rounds were No-Cap, and the distributions of P3 strategies resemble the pooled distribution in ORDERED, where strategies are distributed more in the interior of the interval. A disproportionate amount of corner strategies are also used by P4 in these rounds in Session 3 of MIXED. However, P4 also adopts a disproportionate amount of corner strategies in Session 2, but not Session 1. Although three of these first eight rounds were No-Cap in these Sessions, this difference may be due to the fact that the first trial round was a High-Cost round in Session 2, while it was a No-Cap round in Session 1. In an effort to explain what determines whether subjects satisfy basic rationality, I study their academic records including subjects’ American College Test (ACT) scores, Scholastic Aptitude Test (SAT) scores and major field of study, which were obtained by subjects’ consent from the Ohio State University registrar’s office. ACT scores were obtained for

69 Figure 2.9: Strategies with No Capacity Constraint, Rounds 1-6 of MIXED/ORDERED

Player 3 Player 4

66.9% of subjects, while SAT scores were obtained and SAT-ACT concordance scores used for another 20.5% of subjects.61 Summary statistics on these test scores are reported in Table 2.6. I test for a relationship between these academic records and whether a subject satisﬁes basic rationality using probit regressions with a dependent variable taking on 1 as its value if a subject satisﬁes basic rationality and 0 otherwise. Explanatory variables include indica- tors for whether a subject has an ACT or SAT-ACT concordance score in the top 5% of all test-takers, below the top 20% of all test-takers, or no score reported and an indicator for having a quantitiative major, including math, science, engineering and economics. ACT percentile is the appropriate measure because ACT scores are based on a rank-order scale and

61See http://professionals.collegeboard.com/profdownload/act-sat-concordance-tables.pdf for SAT-ACT concordance tables.

70 Table 2.6: ACT and SAT-ACT Concordance Score Summary Statistics Median 27 Mean 27.58 Std. Err. 0.289 with ACT 66.9% with SAT Only* 20.5% with No Score 12.7% in Top 5% 18.7% below Top 20% 23.5% *SAT-ACT concordance scores used.

not an additive scale. Table 2.7 shows the results of separate probit regressions for P3 and P4.

Result 3.4: Having an ACT or SAT-ACT concordance score in the top 5% of all test-takers makes a Player 4 subject signiﬁcantly more likely to satisfy basic rationality.

For P3, I find no significant relationship between test scores or major and basic rationality. For P4, however, having a test score in the top 5% of all test-takers raises the probability of basic rationality by 26.3 percentage points, and the estimate is significant at the .1 level.62 These test scores have been shown by Frey and Detterman (2004) and Koenig et al. (2008) to be strongly correlated with cognitive ability.63 Hence, I find evidence that the likelihood of meeting the basic rationality benchmark in rounds with no capacity constraint is correlated

62Probit regressions using only test scores or only major as explanatory variables do not yield important diﬀerences from the results of the regressions including all of the explanatory variables presented in Table 2.7. 63This is one of only a few studies in the experimental economics literature to use veriﬁed ACT or SAT scores (as opposed to self-reported scores) as a measure of cognitive ability. See Benjamin and Shapiro (2005), Casari et al. (2007) and Ivanov et al.(2009, 2010) for other examples.

71 Table 2.7: Probits Reporting Marginal Eﬀects of ACT/Major on Satisfying Basic Rationality

Player 3 Player 4 Variable Estimate (S.E.) Estimate (S.E.) Score in Top 5% 0.236 (0.137) 0.263* (0.129) Score below Top 20% 0.078 (0.136) -0.024 (0.142) No Score Reported 0.357** (0.130) 0.123 (0.169) Quantitative Major 0.016 (0.153) 0.071 (0.149) Observations 83 83

with cognitive ability for P4.64 Result 3.3 shows significant treatment effects among BR subjects where such effects are lacking when including non-BR subjects. Together, these results suggest that P4 subjects with relatively high cognitive ability are more likely to respond to the capacity constraint and waiting cost as predicted by the RNBNE when it requires reasoning no deeper than Level-3. For P3, no evidence of a relationship between cognitive ability and basic rationality is found, but there is also little difference between treatment effects observed among BR subjects and in the full data.

2.5.3 Rationality vs. Bounded Rationality

I now consider how well the three theoretical benchmarks discussed in Section 2.3, RNBNE, Level-1 (L1) and Level-2 (L2), ﬁt with the behavior observed in this experiment. To test the ﬁt of these theories with the data, I calculate the mean squared deviation (MSD) of each subject’s strategies in each setting from each of the three theoretical predictions.

Question 4: Are bounded rationality benchmarks better predictors of behavior than the RNBNE?

64This result is consistent with the ﬁndings of Ivanov et al.(2009, 2010) that subjects in their endogenous- timing investment experiment with high SAT scores are more likely to respond as predicted to informational externalities.

72 In contrast to the standard herding model, the model on which this experiment is based affords the advantage of a relatively clear distinction between rational and boundedly-rational benchmarks in their predicted reponses to the capacity constraint and waiting cost. That P4’s L1 High-Cost strategy is to choose contrary to P3 unconditional on his private signal but his RNBNE High-Cost strategy is to follow P3 unconditional on his signal is a feature of the model which provides a particularly clean distinction between boundedly rational and fully rational play. Hence, this experimental design is well-suited for a test of the relative predictive power of these theories and their within-subject robustness across different settings. To test for differences in the goodness-of-fit of each theory, I arrange subject MSDs into a distribution for each theoretical benchmark in each treatment and setting. A distribution with more mass at small MSDs indicates that the corresponding theory is a better fit in that treatment and setting than a distribution with more mass at large MSDs. Differences in these distributions are tested for statistical significance using Kolmogorov-Smirnov tests.65 The MSD distributions are shown for P3 and P4 in Figures 2.10 and 2.11, respectively. Because P3 makes choices following two computer players whose decision rules are fixed and publicly known, but P4 makes choices after observing only the choice of a human P3 whose rationality and decision rule are obviously much more ambiguous, other things equal I would expect that P3’s strategies should exhibit a smaller MSD relative to the RNBNE than P4’s. Subjects’ behavior exhibits a high amount of noise in general, but P3’s behavior is indeed significantly less noisy than P4’s. Across all treatments and settings, the P3 has a mean MSD from the RNBNE of 1627, which is significantly less than P4’s mean MSD from the RNBNE of 2281 according to a Wilcoxon rank-sum test (p < .001). In fact, none of the three theoretical benchmarks provide a very close fit with observed behavior, as less than 45% of P3 subjects and less than 35% of P4 subjects have a MSD less than 500 in every

65Due to the fact that MSDs may exceed 2500 in some cases and not others, in cases where they may exceed 2500 the support of the MSD distribution is truncated to [0,2500] for the Kolmogorov-Smirnov tests. In such cases, MSDs exceeding 2500 are set equal to 2500.

73 Figure 2.10: Player 3 Mean Squared Deviation from Equilibrium

74 Figure 2.11: Player 4 Mean Squared Deviation from Equilibrium

75 treatment/setting combination. However, it is unclear whether this difference between P3 and P4 is due to the computer players or the difference in the complexity of the third and fourth players’ decision problems. Due to the high amount of noise, P3 strategies show little difference in the goodness-of-fit of the theoretical models. L1 fits better than RNBNE (p = .015) and L2 (p = .071) with P3’s No-Cap strategies in ORDERED, but RNBNE fits better than L1 (p = .071) with P3’s Low-Cost strategies in ORDERED. All three theories make the same prediciton for High- Cost P3 strategies, so no comparison is possible in this setting for P3.

Result 4: Player 4 strategies with no capacity constraint ﬁt better with Level-1 than RNBNE. Player 4 strategies with a capacity constraint and high waiting cost ﬁt better with Level-2 than Level-1.

Although they exhibit a high amount of noise, P4 strategies provide some grounds for comparison of the theoretical benchmarks due to the large difference between them in some cases. L1 fits with P4’s No-Cap strategies significantly better than RNBNE in all three treatments (p-values of .020, .015 and .008 in MIXED, ORDERED and NAIVE-MIXED, respectively). This finding is consistent with the common observation in herding experiments that subjects rely more on their private signal than is rational. However, L2 fits significantly better than L1 with P4’s High-Cost strategy in ORDERED (p = .033) and in NAIVE-MIXED (p = .003), where the L2 prediction is very close to the RNBNE. These results lend support to L2 as the best theory of herding behavior with capacity constraints, but overall none of the three theories provides a close fit due to the high amount of noise.

Question 5: Do theoretical predictions explain individual behavior across settings?

76 Table 2.8: Transition Matrix Showing Player 3 Best-Fitting Theory Across Settings

No-Cap Min. MSD Low-Cost Min. MSD (MSD≤1000) RNBNE L1 L2 MSD>1000 Total RNBNE 2 4 1 6 13 L1 10 4 10 1 25 L2 1 1 2 2 6

Table 2.9: Transition Matrix Showing Player 4 Best-Fitting Theory Across Settings

No-Cap Min. MSD Low-Cost Min. MSD High-Cost Min. MSD (MSD≤1000) RNBNE L1 L2 MSD>1000 RNBNE L1 L2 MSD>1000 Total RNBNE 0 0 0 3 1 0 0 2 3 L1 8 7 11 8 7 4 9 14 34 L2 6 1 1 2 4 0 1 5 10

Despite the high amount of noise in the data overall, the experimental design allows me to test for within-subject consistency in the best-fitting theory across settings. Tables 2.8 and 2.9 display transition matrices which compare the best-fitting benchmarks with individual subjects’ strategies in the No-Cap setting to the best-fitting benchmarks with their strategies in settings with a capacity constraint. I restrict attention to subjects whose smallest MSD from one of the No-Cap theoretical benchmarks is not greater than 1000, indicating a reasonable level of consistency in strategies across decisions in this setting. The number of such subjects whose No-Cap strategies fits best with each theory is tallied along with the best-fitting theory for each of these subjects’ strategies in other settings, if the MSD of their strategies from the best-fitting theory in other settings is not greater than 1000. A comparison with High-Cost strategies is not included for P3 because all three benchmarks coincide in this setting.

77 Result 5.1: Of subjects whose strategies ﬁt best with a particular theoretical benchmark without a capacity constraint, no more than one-third use strategies that ﬁt best with the same theoretical benchmark with a capacity constraint.

Tables 2.8 and 2.9 show that the majority of subjects whose No-Cap strategies are reasonably consistent and close to a theoretical benchmark conform most closely to the L1 prediction. However, less than 21% of these subjects use Low-Cost or High-Cost strategies which also fit best with L1. A similar trend obtains among subjects whose No-Cap strategies are reasonably consistent and closest to RNBNE or L2. Hence, I find little evidence that any of these three benchmarks wield much predictive power across settings in this experiment. Some interesting findings emerge when I investigate relationships between subjects’ academic records and the proximity of their strategies to theoretical benchmarks. Table 2.10 reports the results of OLS regressions testing for such relationships for each equilibrium concept, with a subject’s MSD from the particular equilibrium across all her strategies as the dependent variable and the same explanatory variables used in the probit regressions presented in Table 2.7 of Section 2.5.2.

Result 5.2: For Player 3, having a quantitative major signiﬁcantly reduces mean squared deviation from the RNBNE (but also Level-1 and Level-2) across settings.

The regressions for Player 3 indicate that having a quantitative major (defined as math, science, engineering or economics) significantly reduces a subject’s MSD from RNBNE. Be- cause L1 and L2 are relatively close to RNBNE for P3, having a quantitative major also significantly reduces a subject’s MSD from those benchmarks. ACT/SAT test scores do not significantly affect P3’s MSD from any of the equilibria, and when either test scores or major is dropped from the estimated equation, the effect of the remaining variable does not

78 Table 2.10: Relationship Between Test Scores/Major and MSD Scores - OLS Regressions

MSD-RNBNE MSD-L1 MSD-L2. Variable Estimate (S.E.) Estimate (S.E.) Estimate (S.E.) Player 3 Score in Top 5% -185.2 (282.2) -259.5 (305.2) -168.7 (263.6) Score below Top 20% 206.6 (253.5) 198.3 (274.2) 144.6 (236.8) No Score Reported -75.5 (326.7) 85.7 (353.3) -39.5 (305.1) Quantitative Major -520.1* (271.5) -725.9** (293.6) -461.1* (253.5) Constant 1707.3*** (153.1) 1632.0*** (165.6) 1616.5*** (143.0) Observations 83 83 83 Player 4 Score in Top 5% -801.7** (394.4) 746.9* (440.8) 216.2 (278.1) Score below Top 20% -557.1 (376.7) -15.7 (421.1) -132.3 (265.6) No Score Reported -586.5 (472.8) -236.4 (528.5) -334.8 (333.3) Quantitative Major 166.5 (398.5) 234.1 (445.4) 152.6 (280.9) Constant 2610.9*** (220.7) 2250.2*** (246.7) 1734.3*** (155.6) Observations 83 83 83

change in signiﬁcance. This result is interesting because P3’s task is essentially a one-person decision problem, as her payoﬀs and information are determined entirely by hers and the computer’s decisions and she does not interact with other human players in any important way. The result suggests that P3’s ability to comprehend the rules of the game and determine a best-response given its entirely mechanical nature, i.e., the subject’s “technical literacy,” is a more important determinant of her proximity to any of the equilibria than a test score highly correlated with cognitive ability.

Result 5.3: For Player 4, having an ACT or SAT-ACT concordance score in the top 5% of all test-takers signiﬁcantly decreases mean squared deviation from RNBNE and signiﬁcantly increases mean squared deviation from Level-1 across settings.

79 In contrast with the P3 results, having a quantitative major does not significantly affect P4’s MSD from theoretical predictions. However, having an ACT/SAT score in the top 5% of all test-takers makes P4’s MSD from RNBNE significantly smaller and her MSD from L1 significantly larger. There is no significant relationship between test scores and MSD from L2. These results are robust to the exclusion of major as an explanatory variable, and dropping the test score variables does not produce a significant relationship between major and MSD. Result 5.3 provides an explanation for the dichotomy of P4 behavior present in the data. The High-Cost RNBNE prediction (follow P3 unconditional on the private signal) and L1 prediction (choose contrary to P3 unconditional on the private signal) are at opposite extremes, and across treatments I observe a substantial amount of strategies consistent with each. This result suggests that those with high cognitive ability tend to use strategies closer to the fully rational prediction and farther from the L1 prediction. That major does not explain proximity to the equilibria but test score does suggests that technical literacy is not enough to explain P4 performance. P4 faces a problem beyond simply comprehending the rules of the game; he must also make inferences about unseen information from the observed choice of a human player, P3. Therefore, it is not suprising that a P4 with high cognitive ability would be more likely to perform the deeper reasoning necessary to arrive at the RNBNE strategy and less likely to behave as if he believes P3 chose randomly.

2.6 Conclusion

This study contributes to the herding literature by investigating behavior in environments where the available options are subject to capacity constraints. The model predicts and results of the experiment conﬁrm that capacity constraints can attenuate herding behavior, with the size of the eﬀect dependent on the penalty of choosing an option after its capacity has been reached. However, whether subjects later in a sequence of choices respond rationally

80 to the capacity constraint is found to be dependent on factors such as the depth-of-reasoning involved in the fully rational equilibrium and the subject’s cognitive ability. Results of the experiment provide evidence that limited depth-of-reasoning is an important factor in herding behavior but little support for the idea that the chance of errors by preceding players is responsible for departures from equilibrium. Subjects choosing later in a sequence with high cognitive ability, as evidenced by ACT/SAT scores, are more likely to satisfy a basic rationality benchmark and tend to use strategies closer to the Risk-Neutral Bayesian Nash Equilibrium strategy and farther from the boundedly rational Level-1 strategy. Those who satisfy the basic rationality benchmark respond to the capacity constraint as predicted given that the Risk-Neutral Bayesian Nash Equilibrium requires reasoning no deeper than Level-3. Among subjects choosing earlier in a sequence, whose predecessors are computers rather than humans, no such tendencies are found as behavior generally conforms to rational predictions. Athough their predecessors are computers whose choice rules are ﬁxed and commonly known, their strategies do not diﬀer markedly from those in previous experiments where predecessors are human subjects.

81 Chapter 3: eBay Auctions of Amazon.com Gift Certiﬁcates: A Study of Bidding Fever in the Field

3.1 Introduction

Auctions of Amazon.com gift certificates offer a unique view of bidding behavior because the outside option for purchasing the certificates at face value is particularly prominent. I study 506 auctions of these certificates completed on eBay between 9/1/2008 and 10/28/2008. In 41.1% of these auctions, the winning price exceeds the face value, which is an upper bound for rational bidding. Limited attention to alternatives is not a likely explanation for this overbidding because it is reasonable to assume that anyone interested in acquiring a certificate would be aware that they can be purchased at face value directly from Amazon.com with negligible transaction costs. Bidding fever, defined as the expectation of extra utility from winning an auction that is inspired during the bidding process66, is a more plausible explanation for the overbidding I observe, and additional features of the data are consistent with it.

82 Table 3.1: Descriptive Statistics Face Value Price Paid by Winner # of Bids Winner’s Bidder Rating Mean $58.04 $56.92 7.4 780 Median $25.00 $25.31 6.0 60 Max $573.45 $559.24 50 20453 Min $5.00 $4.25 1 0

3.2 Data

Amazon.com gift certificates can be purchased at face value through a prominent link at the top of the Amazon.com homepage. The option for free shipping or email delivery is clearly visible. A purchase can be completed in less than 5 minutes by anyone with minimal web browsing capabilities. Hence, the transaction costs involved in acquiring the certificates directly from Amazon.com are negligible, making the face value the upper bound for rational eBay bids. eBay.com auctions use a modified second-price sealed-bid format. They have a fixed, publicly known end point, until which all bidders may bid repeatedly. The highest bidder wins and pays the second-highest bid plus a minimum bid increment. Summary statistics for the certificate face value, price paid by the winning bidder, number of bids placed on the item, and winner’s bidder rating for the auctions studied67 are reported in Table 3.1. Though the face value of a certificate is the upper bound for rational bidding, 41.1% of the auctions end with a price greater than face value. Much of the overbidding is non-negligible, as 14.6% of winning prices exceed face value by more than $1, and 10.1% of winning prices

66The closely related idea of utility of winning refers to a constant extra utility derived from winning, rather than a temporary one as in bidding fever. Because they would be observationally equivalent in the data, I discuss bidding fever while acknowledging that utility of winning is equally plausible. 67Buy-it-now and best-oﬀer sales are excluded from the sample.

83 Table 3.2: Summary of Overbidding # (out of 506 obs.) % of obs. Overbid 208 41.1% Overbid by >$1 74 14.6% Overbid by >$5 27 5.3% Overbid by >5% 71 14.0% Overbid by >10% 51 10.1%

are at least 10% greater than face value. Table 3.2 reports overbidding statistics.68 I exclude shipping costs when calculating overbidding because sellers required the winner to pay for shipping in only 11 of the auctions in the data. A payment exceeding the face value of the certiﬁcate would exceed it by a greater margin with shipping included. I also observe the time and date at which each auction ended, summarized in Table 3.3. The majority of auctions ended between the hours of 12 pm and 8 pm Eastern Time, and these auctions exhibit a higher frequency of overbidding than auctions ending at other times. The days of the week with the greatest numbers of auctions ending were Sunday, Monday and Tuesday. The majority of auctions ended within these three days of the week, and these auctions exhibit a lower frequency of overbidding than auctions ending later in the week.

3.3 Interpretation

The rate of overbidding in these auctions is comparable to that observed by Lee and Malmendier (2011) in eBay auctions of a cross-section of items. They find that 48% of winning prices in these auctions exceed fixed prices for the same item listed nearby on eBay. Although they cannot rule out bidding fever or utility of winning, they find evidence suggesting that bidding more than the fixed price occurs because that alternative is ignored or

68Categories in Table 3.2 are not mutually exclusive.

84 Table 3.3: Overbidding by Time and Day of Week Auctions Overbid % Overbid 4am-12pm ET 155 61 39.4% 12pm-8pm ET 265 113 42.6% 8pm-4am ET 86 34 39.5% Monday 77 29 37.7% Tuesday 82 29 35.4% Wednesday 50 24 48.0% Thursday 51 21 41.2% Friday 75 36 48.0% Saturday 75 33 44.0% Sunday 96 36 37.5%

forgotten. This is an unlikely explanation for the overbidding I observe given the prominence of the outside option (buying certificates from Amazon.com). Lee and Malmendier also report survey data suggesting that bidding fever does occur in eBay auctions. I find additional features of the data that are consistent with bidding fever. Because 241 of the 506 auctions (47.6%) end in a price below face value, bidders may enter an auction seeking a discount but overbid because they catch fever during the auction process. Cooper and Fang (2008), Heyman et al. (2004) and Ku et al. (2004) suggest that bidding fever is related to the competitiveness of an auction. I find that overbidding is more common when there is a high number of bids placed on a certificate, as the price exceeds face value by more than $1 in 6.4% of the 267 auctions with six or less bids and in 23.8% of the 239 auctions with more than six bids. A one-tailed t-test shows that this difference in proportions is statistically significant (p-value < .0001). One must be careful not to interpret this fact as definitive evidence of bidding fever by itself because it is not necessarily a prediction of all bidding fever models, and it could also be consistent with other explanations for overbidding. Nevertheless, it is noteworthy because the cited literature suggests a correlation between competitiveness and overbidding due to bidding fever.

85 Table 3.4: Overbidding and Winning Bidder’s Rating Bidder Rating Auctions Overbid % Overbid 0-9 98 54 55.1% 10-29 88 44 50.0% 30-129 85 35 41.2% 130-499 96 37 38.5% 500+ 110 26 23.6% Total 477 196 41.1%

Chan et al. (2007) and Garratt et al. (2008) suggest the plausible hypothesis that experienced bidders are less susceptible to bidding fever. The bidder ratings in my data provide evidence that is consistent with this prediction. The winning bidders rating is observed for 477 of the auctions69. At the time when the data was collected, a point was added to a rating for positive feedback from a seller and a point was subtracted for negative feedback, so a low rating does not necessarily imply that the bidder is inexperienced. However, bidders with a high rating must be experienced, so I expect a relatively low rate of overbidding among these bidders if, as seems plausible, experienced bidders are less susceptible to bidding fever. Table 3.4 partitions the data into bins by bidder rating and reports the overbidding frequency in each. A negative relationship is evident. A median split of the auctions by winning bidder’s rating shows that the price exceeded the face value by more than $1 in 20.4% of the 240 auctions where the rating is 60 or less and 7.5% of the 239 auctions where it is greater than 60. A one-tailed t-test shows that this difference is statistically significant (p-value < .0001). The magnitude of overbidding is also negatively related to the bidder rating, as the correlation between the winning price’s percentage difference from face value and the winning bidder’s rating is negative (coefficient = -.0739) and marginally significant (p-value = .0536).

69Some bidders had an unobservable private rating.

86 3.4 Alternative Interpretations

An alternative explanation is that winning bidders somehow avoid paying the full auction price. Because the overall frequency of overbidding is so large and the frequency remains substantial among bidders with a high rating (see Table 3.3), fraudulent bidders who overbid but default on payment are not likely to account for much of the observed behavior. I am aware of two promotional discounts that were offered during these auctions which may explain some of the overbidding. A cash-back rebate was offered on buy-it-now purchases from eBay listings accessed through a Microsoft Live.com search. This promotion did not apply to auctions, but it was advertised for buy-it-now listings among the listings of auctions for similar items. Some bidders may have misunderstood the terms of the discount, mistakenly believing it to apply to auctions as well. However, the promotion was only sporadically advertised, and for it to account for a large proportion of the overbidding would require rather massive misunderstanding. An eBay Mastercard promotion appeared during auctions with a bid over $50 offering bidders the opportunity to defer payment for 3-4 months with no interest if the item became their first eBay purchase with that card. The promotion did not apply to auctions ending with a price of $50 or less. Overbidding occurred in 47.8% of the 157 auctions to which the promotion applied, compared to a 38.1% rate in the rest of the auctions. A one-tailed t-test shows that this difference is statistically significant (p-value = .0205), so bidders showed a greater tendency to overbid when they could take advantage of this promotion. However, a substantial amount of overbidding still occurred when they could not. Transaction costs involved in purchasing certificates from Amazon.com which can be avoided through an eBay purchase could also rationalize overbidding. However, the ease of acquiring certificates directly from Amazon.com generally rules this out. Even when eBay bidders pursue a bargain on a certificate but the auction price eventually rises above face

87 value, the minimal amount of time and effort needed to switch to a cheaper Amazon.com purchase should not discourage them from doing so. After all, extra time and effort could not be too costly for people who are willing to participate in the auction. Because Amazon.com only accepts U.S. credit cards or checking accounts for payment, it may be rational for bidders outside the U.S. to pay more than face value for a certificate through eBay, where other payment methods can be used. To address this possibility, I collected a small sample of new data, consisting of 95 eBay auctions of Amazon.com gift certificates completed between 7/15/2010 and 7/30/2010. 50 of these auctions ended in a price greater than face value. Unlike the original data, this data includes the location of each auction winner. 83 of the auctions in this sample were won by a bidder inside the U.S., and 42 of those ended in a price greater than face value. Therefore, unless the population and behavior of bidders in auctions for these certificates changed drastically between 2008 and 2010, foreign bidders are unlikely to account for much of the overbidding in the original data. It remains possible that bidders inside the U.S. without a credit card or checking account are responsible for the overbidding, but this is unlikely to account for much of it.

3.5 Regression Analysis

To more precisely test for the relationship between overbidding and other variables in the data, I conduct OLS regressions with percentage overbid, defined as the difference between the winning bid and the face value expressed as a percentage of the face value, as the dependent variable and the following explanatory variables. The number of bids placed on the item (bids) is included as a measure of the competitiveness of the auction. The face value of the certificate (face) is included to test for a relationship between the value of the gift certificate and the proportion of overbidding. I also include a variable to account for any discontinuity in the relationship between face value and overbidding due to the eBay Mastercard promotion for purchases of $50 or more. This term is the product of a variable

88 Table 3.5: OLS Regression - Dependent Variable: Percentage Overbid Estimates Reported in Terms of Percentage Points (x.xxx% of Face Value) Speciﬁcation w/ Bidder Rating w/o Bidder Rating Variable Estimate (Std. Err.) Estimate (Std. Err.) bids 0.263*** (0.092) 0.293*** (0.091) lograting -0.708*** (0.165) —— face -0.083*** (0.029) -0.074*** (0.028) disc*fd 0.076** (0.031) 0.068** (0.031) date -0.002 (0.024) -0.017 (0.024) aft 2.174** (0.915) 2.228** (0.911) eve -0.427 (1.205) -0.214 (1.208) latewk 1.874** (0.801) 1.880** (0.799) constant 1.405 (1.426) -1.797 (1.219) Observations 477 506

equal to the face value of the certiﬁcate minus 49.99 (fd), and a dummy variable taking on 1 as its value if the promotion applied and 0 otherwise (disc). I include dummy variables for time of day indicating whether the auction ended between 12 pm and 8 pm ET (aft) or whether the auction ended between 8 pm and 4 am ET (eve), with auctions ending between 4 am and 12 pm ET as the omitted category.70 I also include an indicator variable for time of the week (latewk) which has a value of 1 if the auction ended between Wednesday and Saturday and 0 otherwise. The number of days elapsed between a given auction’s closing and the day I began collecting data (date) is also included to account for any time trend in the proportion of overbidding over the period in which the data was collected. I use two speciﬁcations, one which includes as an explanatory variable the log of the winner’s bidder rating plus 1 (lograting) as a measure of the winner’s eBay experience, and one which does not. All of the other explanatory variables described above are included in

70Though I cannot account for time diﬀerences between the Eastern zone and the bidder’s actual location, the majority of eBay bidders are located in the U.S., so these three blocks of Eastern time should be a rough approximation of the time of day for the majority of bidders.

89 both specifications. Because the bidder rating of the winner was private in 29 of the auctions in the data, these auctions are included only in the regression without bidder rating as an explanatory variable. The results of these regressions are presented in Table 3.5. The estimates of interest to the bidding fever interpretation, the effect of number of bids and bidder rating on percentage overbid, are significant and have the expected sign. The number of bids placed on the item, which is a measure of the competitiveness of an auction, has a small but significant positive effect on percentage overbid. The log of the bidder rating has a significant negative effect, indicating that more experienced bidders are less likely to overbid. Thus, this regression analysis supports the aggregate characteristics of the data that are consistent with a bidding fever interpretation of the observed overbidding. I find that face value has a significant negative effect on the proportion of overbidding, indicating that bidders tend to overbid by a smaller proportion on gift certificates with larger face values among those ineligible for the eBay Mastercard promotion at face value. However, this tendency is nullified for certificates with a face value of $50 or greater, for which a bid at or above face value would qualify for the promotion. Interestingly, percentage overbid is significantly increased during the afternoon/early evening hours of Eastern time compared to the morning hours, but no significant effect is observed for late-night hours. In addition, compared to auctions ending on Sunday through Tuesday, percentage overbid is significantly greater later in the week. These estimates indicate that greater overbidding occurs at times when U.S. bidders may be more likely to participate in auctions for recreational purposes, which may make bidding fever more likely.

3.6 Conclusion

Though one can never rule out all possible rational explanations for the behavior doc- umented here, I have addressed all that seem relevant and can be addressed with the data

90 available. Auctions of Amazon.com gift certificates were purposefully chosen for study because of the negligible transaction costs of purchasing certificates from Amazon.com and the prominence of this outside option, which eliminate many of the usual explanations for overbidding such as limited attention to alternatives. Bidding fever cannot be ruled out, and indeed, seems like the most plausible explanation. I define bidding fever as the expectation of extra utility from winning an auction that is somehow inspired during the bidding process, but I do not espouse any augmented model of bidding fever which details how that expectation is formed. I present these findings as evidence which strongly suggests that bidding fever exists and poses an important challenge to those who are skeptical of its existence.

91 Appendix A: Appendix to Strategic Complexity and Cooperation: An Experimental Study

A.1 Directed Graph Representations of Selected Automaton Strate-

gies in Each Treatment

Nodes represent the states of the automaton, which are labeled by the action number output of the behavior function when taking that state as the input. The circled node is the initial state. Edges represent the state transition function mapping from the input state and the opponent action or the payoﬀ table announcement to the output state.

Figure A.1: Always Defect (AD)

92 Figure A.2: Always Cooperate (AC)

Figure A.3: Grim Trigger (GT)

93 Figure A.4: Tit-for-Tat (TFT)

A.2 Instructions and Screenshots

Instructions for the SWITCH-C treatment are reprinted below. The instructions for NOSWITCH and SWITCH-D are identical except for the payoﬀ tables. The NOSWITCH- R instructions are similar except that the experiment is initially described in the context of the multiple game phase.

A.2.1 Phase I Instructions

This is an experiment in the economics of decision making. If you follow these instructions carefully and make good decisions you may earn a considerable amount of money which will be paid to you in cash at the end of the experiment. The experiment is divided into rounds. In each round, you will be matched randomly and anonymously with another person in the room, and you will remain matched with the same person for the duration of that round. When a round ends, you will be randomly matched with another person for a new round.

94 Rounds are divided into periods. Each round lasts for a random number of periods. After every period, the round has a 80% chance of continuing. This is as if in each period a ball is drawn randomly from a container with 4 red balls and 1 black ball, and the round continues if a red ball is drawn and ends if the black ball is drawn. You will be asked to make a choice (1, 2, or 3) in each period, as will the person with whom you are matched. Your payoff in that period depends on your choice, the choice of the other person, and the payoff table in use during that period. Remember that you are matched with the same person for every period until the round ends. Payoffs are denominated in experimental currency units (ECUs). In each period, one of the following two payoff tables will be used:

The first number in each cell of a table is your payoff, while the second number is the payoff of the other person. For example, suppose that table Y is in use in the current period. If you choose 1 and the other person chooses 1, you each make 45 in that period. If you choose 2 and the other person chooses 3, you make 0 while the other person makes 10. If you choose 3 and the other person chooses 1, you make 60 while the other person makes 5. Before each period, the payoff table we will use in that period is drawn randomly. Each table has a 50% chance of being used in each period. This is as if a coin is flipped before

95 each period, and the table we will use in that period is Y if it comes up heads and Z if it is tails. At the beginning of every round, you will be able to view the payoff table we will use in the first period of the round by clicking a button on your computer screen. At this point you should pay attention to which of the two payoff tables will be used in the first period and think about what choice you will make. It is important to plan ahead because this payoff table information will not remain on the screen after you click “OK (although you can always refer to the tables in these instructions). After this initial screen in the first period, you will be presented with a series of three screens. These three screens will appear again in the same order in every period of the round. 1. The first screen asks for your choice in the current period (1, 2, or 3). After the first period of a round, your choice from the previous period will appear as a default choice, and the same choice will be entered in the current period if you do not change it. Click “OK to confirm your choice. 2. The second screen includes a button you can click to view the payoff table we will use in the next period if the round continues after the current period. For example, if it is currently period 3 then clicking the button reveals the payoff table that we will use in period 4 if this round advances to period 4, which it has a 80% chance of doing. At this point you should pay attention to which of the two payoff tables we will use in the next period and plan ahead. After you click “OK and advance past this screen, payoff table information for the next period will not appear again before you make your choice in the next period. 3. The third screen reports the payoff table used in the current period, your choice from the current period, the other persons choice from the current period, and your payoff from the current period. Your cumulative payoff for the round is also shown. To keep the experiment moving, each of these screens will be viewable for a maximum of 20 seconds, for a total time limit of 60 seconds per period. After the third screen is viewed,

96 the round either continues to the next period or ends. Remember that after each period the round has a 80% chance of continuing and a 20% chance of ending. You remain matched with the same person in every period of a round, but when the round ends you will be randomly re-matched with another person for the next round. There will be one practice round like this, and then we will begin playing for cash. At the midpoint of this session, we will pass out additional instructions. In the second half of the experiment, you will participate in four matches simultaneously in each round. For now, you will only be matched with one person per round. At the end of the experiment, you will be paid $0.004 for every ECU earned in the experiment plus the show-up fee of $6.

A.2.2 Phase II Instructions

In each round of the second half of the experiment, you will participate in four separate matches simultaneously. Matches are color-coded (Blue, Green, Red, and Yellow). The person you are matched with for each color is random and independent of whom you are matched with for the other colors. For each color, you remain matched with the same person in every period of a round. As in the first half of the experiment, each round lasts a random number of periods. After every period, the round has a 80% chance of continuing. When the round ends, you will be randomly and independently re-matched with another person for each color in the next round. In each period of a round, you will be asked to decide between three choices for each of the four colors. You are free to make any choice you want for each color. Your payoff for each color in that period depends on your choice for that color, the choice of the person with whom you are matched for that color, and the payoff table in use for that color during that period. Payoff tables are drawn randomly and independently for each color before every period. This means that the payoff table used may differ between colors in the same period.

97 The two possible payoff tables (Y and Z) are the same as before, and each table has a 50% chance of being used for each color in each period. At the beginning of every round, you will be able to view the payoff table we will use for each color in the first period by clicking the corresponding button on your computer screen. At this point you should pay attention to which payoff tables will be used in the first period and plan ahead because payoff table information will not remain on the screen after you click “OK. After this initial screen in the first period, you will be presented with a series of three screens. These three screens will appear again in the same order in every period of the round. 1. The first screen asks for your choice in the current period (1, 2, or 3) for each color. 2. The second screen includes four buttons, one for each color. You can click these buttons to view the payoff table we will use for the corresponding color in the next period if the round continues after the current period. At this point you should pay attention to which payoff tables will be used in the next period and plan ahead. After you click “OK and advance past this screen, the payoff table information for the next period will not appear again before you make your choices in the next period. 3. The third screen reports for each color the payoff table used in the current period, your choice from the current period, the other persons choice from the current period, and your payoff from the current period. Your cumulative payoff for the round from all four colors is also shown. Each of these screens will be viewable for 20 seconds, for a total time limit of 60 seconds per period. After the third screen is viewed, the round either continues to the next period or ends.

98 Figure A.5: Screen 1 (Single Game Rounds)

99 Figure A.6: Screen 2 (Single Game Rounds)

100 Figure A.7: Screen 3 (Single Game Rounds)

101 Figure A.8: Screen 1 (Multiple Game Rounds)

102 Figure A.9: Screen 2 (Multiple Game Rounds)

103 Figure A.10: Screen 3 (Multiple Game Rounds)

104 Appendix B: Appendix to An Experiment on Herding with Capacity Constraints

B.1 Derivation of RNBNE

Suppose xn−1 = R. Risk-neutral player n chooses alternative R if and only if the following holds: P4 i=1 θi E[ 4 − Cn(x1, ..., xn−1,R)|θn, xn−1 = R] P4 i=1 θi ≥ E[1 − 4 − Cn(x1, ..., xn−1,L)|θn, xn−1 = R].

1 Because θn+1, ..., θ4 are independent with mean 2 , this inequality can be re-written as,

Pn−1 1 i=1 θi+θn+ 2 (4−n) E[ 4 − Cn(x1, ..., xn−1,R)|θn, xn−1 = R] Pn−1 1 i=1 θi+θn+ 2 (4−n) ≥ E[1 − 4 − Cn(x1, ..., xn−1,L)|θn, xn−1 = R], which simpliﬁes to:

n−1 n X θ ≥ − E[ θ − 2(C (x , ..., x ,R) − C (x , ..., x ,L))|x = R]. n 2 i n 1 n−1 n 1 n−1 n−1 i=1

Hence, player n uses a cutoﬀ strategy given by:

  ˆ R if θn ≥ θn xn(xn−1 = R) = ,  ˆ L if θn < θn

105 ˆ n Pn−1 where θn = 2 − E[ i=1 θi − 2(Cn(x1, ..., xn−1,R) − Cn(x1, ..., xn−1,L))|xn−1 = R]. The

problem is symmetric for xn−1 = L, so in this case the player follows a strategy given by:

  ˆ R if θn ≥ 1 − θn xn(xn−1 = L) = .  ˆ L if θn < 1 − θn

I now derive the Risk-Neutral Bayesian Nash Equilibrium (RNBNE) strategies for Players 1 through 4.

Player 1: Because θ2, θ3 and θ4 are drawn independently and uniformly from [0,1], it ˆ 1 follows trivially that θ1 = 2 holds. Player 2: Because neither option’s capacity can be reached after only one player’s choice,

3 E[θ1 − 2(C2(x1,R) − C2(x1,L))|x1 = R] = E[θ1|x1 = R] = 4 holds, which imples that ˆ 3 1 θ2 = 1 − 4 = 4 holds. ˆ ˆ 3 Player 3: By Bayes’ Rule it follows from θ1 and θ2 that P r(x1 = R|x2 = R) = 4 holds. 3 1 Hence, E[θ1 + θ2|x2 = R] = 4 E[θ1 + θ2|x1 = x2 = R] + 4 E[θ1 + θ2|x1 = L, x2 = R] = 3 5 6 1 7 2 21 3 6c 4 ( 8 + 8 ) + 4 ( 8 + 8 ) = 16 holds. Also, E[2(C3(x1,R) − C3(x1,L))|x2 = R] = 2 4 c = 4 holds. ˆ 3 21 6c 3+24c 3+24c Therefore, θ3 is equal to the minimum of 2 − 16 + 4 = 16 and 1 because 16 > 1 implies 3+24c 13 that it is never optimal for Player 3 to follow Player 2. 16 > 1 holds if and only if c > 24 holds.

ˆ ˆ ˆ 13 Player 4: By Bayes’ Rule it follows from θ1,θ2 and θ3 that if c ≤ 24 holds then P r(x2 = 13−24c R|x3 = R) = 16 holds. Hence, we have,

13 where the following hold if c ≤ 24 holds:

106 5 6 19+24c E[θ1 + θ2 + θ3|x1 = x2 = x3 = R] = 8 + 8 + 32 ; 7 2 19+24c E[θ1 + θ2 + θ3|x1 = L, x2 = x3 = R] = 8 + 8 + 32 ; 1 6 29−24c E[θ1 + θ2 + θ3|x1 = x3 = R, x2 = L] = 8 + 8 + 32 ; 3 2 29−24c E[θ1 + θ2 + θ3|x1 = x2 = L, x3 = R] = 8 + 8 + 32 .

473−576c2 Some algebra yields E[θ1+θ2+θ3|x3 = R] = 256 . In addition, we have E[2(C4(x1, x2,R)− 13−24c 1 3+24c 3 3+24c 368c−1152c2 13 C4(x1, x2,L))|x3 = R] = 2( 16 c + 4 16 c − 4 16 c) = 256 . Therefore, if c ≤ 24 ˆ 473−576c2 368c−1152c2 39+368c−576c2 13 holds then we have θ4 = 2 − 256 + 256 = 256 . However, if c > 24 holds, then we have instead:

P r(x2 = R|x3 = R) = 0;

1 6 1 E[θ1 + θ2 + θ3|x1 = x3 = R, x2 = L] = 8 + 8 + 2 ; 3 2 1 E[θ1 + θ2 + θ3|x1 = x2 = L, x3 = R] = 8 + 8 + 2 .

19 In this case, E[θ1 + θ2 + θ3|x3 = R] = 16 and E[2(C4(x1, x2,R) − C4(x1, x2,L))|x3 = R] = 1 3 13 ˆ 19 2( 4 c − 4 c) = −c. Therefore, if c > 24 holds then θ4 is equal to the maximum of 2 − 16 − 13−16c 13−16c c = 16 and 0 because 16 < 0 implies that Player 4 should always follow Player 3. 13−16c 13 16 < 0 holds if and only if c > 16 holds. Individual rationality is satisﬁed trivially for Players 1 and 2 because they never incur the waiting cost and for Player 3 because she can always avoid the cost by choosing contrary to Player 2. For Player 4, the individual rationality condition for choosing alternative L P4 i=1 θi given x3 = R, E[ 4 − C4(x1, x2, x3,R)|θ4, x3 = R] ≥ 0, can be solved for the condition, 473 − 880c + 576c2 ≥ 0, which holds for all c ∈ [0, 1].

B.2 Derivation of Level-k Strategies

˜Lk ˜Lk The Level-k strategies of Players 3 and 4 are denoted by θ3 and θ4 . The Level-1 Player

1 1 n believes that P r(xn−2 = R|xn−1 = R) = 2 and E[θi|xi] = 2 hold for all i < n. For Player

107 1 ˜L1 3, E[2(C3(x1,R) − C3(x1,L))|x2 = R] = 2 2 c = c holds. Hence, θ3 is equal to the minimum 3 1+2c 1+2c of 2 − 1 + c = 2 and 1 because 2 > 1 implies that it is never optimal for Player 3 to 3 1 follow Player 2. For Player 4, E[2(C4(x1, x2,R) − C4(x1, x2,L))|x3 = R] = 2( 4 c − 4 c) = c ˜L1 3 1+2c 1+2c holds. Hence, θ4 is equal to the minimum of 2− 2 +c = 2 and 1 because 2 > 1 implies 1+2c 1 that it is never optimal for Player 4 to follow Player 3. 2 > 1 holds if and only if c > 2 holds.

1 1 The Level-2 Player 3 believes that P r(x1 = R|x2 = R) = 2 , E[θ1|x2] = 2 , E[θ2|x2 = 3 1 R] = 4 and and E[θ2|x2 = L] = 4 hold. It follows that E[2(C3(x1,R) − C3(x1,L))|x2 = R] = 1 ˜L2 3 5 1+4c 2 2 c = c holds. Therefore, θ3 is equal to the minimum of 2 − 4 + c = 4 and 1 because 1+4c 1+4c 4 > 1 implies that it is never optimal for Player 3 to follow Player 2. 4 > 1 holds if 3 and only if c > 4 holds. 1 1 The Level-2 Player 4 believes that P r(x1 = R|x2 = R) = 2 , E[θ1|x2] = 2 , E[θ2|x2 = 3 1 R] = 4 and E[θ2|x2 = L] = 4 hold and that Player 3’s strategy is her Level-1 strategy. 1 1−2c By Bayes’ Rule it follows that if c < 2 holds then we have P r(x2 = R|x3 = R) = 2 , 1 1 and if c ≥ 2 holds then we have P r(x2 = R|x3 = R) = 0. Hence, if c < 2 holds then 1−2c 1+2c we have E[θ1 + θ2 + θ3|x3 = R] = 2 E[θ1 + θ2 + θ3|x2 = x3 = R] + 2 E[θ1 + θ2 + 1−2c c 1+2c 3 c 7−2c−4c2 1 θ3|x2 = L, x3 = R] = 2 (2 + 2 ) + 2 ( 2 − 2 ) = 4 , and if c ≥ 2 holds then we 5 1 have E[θ1 + θ2 + θ3|x3 = R] = 4 . Also, if c < 2 holds then we have E[2(C4(x1, x2,R) − 1−2c 1 1+2c 1 1+2c 2 1 C4(x1, x2,L))|x3 = R] = 2( 2 c + 2 2 c − 2 2 c) = c − 2c , and if c ≥ 2 holds then we 1 1 ˜L2 have E[2(C4(x1, x2,R) − C4(x1, x2,L))|x3 = R] = 2( 2 c − 2 c) = 0. Therefore, θ4 is equal to 7−2c−4c2 2 1+6c−4c2 1 ˜L2 5 3 1 2 − 4 + c − 2c = 4 if c < 2 holds and θ4 is equal to 2 − 4 = 4 if c ≥ 2 holds. In MIXED and ORDERED, the Level-3 Player 4 believes that Players 1 and 2 follow their RNBNE strategies, and that Player 3’s strategy is her Level-2 strategy. By Bayes’

3 3−4c Rule it follows that if c < 4 holds then we have P r(x2 = R|x3 = R) = 4 , and if 3 3 c ≥ 4 holds then we have P r(x2 = R|x3 = R) = 0. Hence, if c < 4 holds then we have 3−4c 1+4c E[θ1 +θ2 +θ3|x3 = R] = 4 E[θ1 +θ2 +θ3|x2 = x3 = R]+ 4 E[θ1 +θ2 +θ3|x2 = L, x3 = R] =

108 3−4c 3 5 6 5 c 1 7 2 5 c 1+4c 1 1 6 7 c 3 3 2 7 c 236−16c−128c2 4 ( 4 ( 8 + 8 + 8 + 2 )+ 4 ( 8 + 8 + 8 + 2 ))+ 4 ( 4 ( 8 + 8 + 8 − 2 )+ 4 ( 8 + 8 + 8 − 2 )) = 128 , 3 5 3 and if c ≥ 4 holds then we have E[θ1 + θ2 + θ3|x3 = R] = 4 . Also, if c < 4 holds then we 3−4c 1 1+4c 3 1+4c 5c−12c2 have E[2(C4(x1, x2,R) − C4(x1, x2,L))|x3 = R] = 2( 4 c + 4 4 c − 4 4 c) = 4 , and 3 1 1 if c ≥ 4 holds then we have E[2(C4(x1, x2,R) − C4(x1, x2,L))|x3 = R] = 2( 2 c − 2 c) = 0. ˜L3 236−16c−128c2 5c−12c2 20+176c−256c2 3 ˜L3 Therefore, θ4 is equal to 2 − 128 + 4 = 128 if c < 4 holds and θ4 is 5 3 3 equal to 2 − 4 = 4 if c ≥ 4 holds. 1 In NAIVE-MIXED, the Level-3 Player 4 believes that P r(x1 = R|x2 = R) = 2 , E[θ1|x2] = 1 3 1 2 , E[θ2|x2 = R] = 4 and E[θ2|x2 = L] = 4 hold and that Player 3’s strategy is her 3 Level-2 strategy. By Bayes’ Rule it follows that if c < 4 holds then we have P r(x2 = 3−4c 3 R|x3 = R) = 4 , and if c ≥ 4 holds then we have P r(x2 = R|x3 = R) = 0. Hence, 3 3−4c if c < 4 holds then we have E[θ1 + θ2 + θ3|x3 = R] = 4 E[θ1 + θ2 + θ3|x2 = x3 = 1+4c 3−4c 1 3 5 c 1+4c 1 1 7 c 58−32c2 R] + 4 E[θ1 + θ2 + θ3|x2 = L, x3 = R] = 4 ( 2 + 4 + 8 + 2 ) + 4 ( 2 + 4 + 8 − 2 ) = 32 , 3 5 3 and if c ≥ 4 holds then we have E[θ1 + θ2 + θ3|x3 = R] = 4 . Also, if c < 4 holds then 3−4c 3 we have E[2(C4(x1, x2,R) − C4(x1, x2,L))|x3 = R] = 2( 4 c, and if c ≥ 4 holds then we 1 1 ˜L3 have E[2(C4(x1, x2,R) − C4(x1, x2,L))|x3 = R] = 2( 2 c − 2 c) = 0. Therefore, θ4 is equal to 58−32c2 3−4c 6+486c−32c2 3 ˜L3 5 3 3 2 − 32 + 2( 4 c = 32 if c < 4 holds and θ4 is equal to 2 − 4 = 4 if c ≥ 4 holds.

B.3 Risk Aversion

I explore the impact of risk-aversion on the Bayesian Nash Equilibrium by solving nu- merically for the equilibrium strategies of Players 3 and 4 under the assumption that the p utility of choice xn is given by U(xn) = π(xn), where π(xn) is the payoﬀ of choice xn and all players 1, .., n − 1 are assumed to behave according to the RNBNE. These strategies are

ˆRA ˆRA ˆRN denoted by θ3 and θ4 and shown below along with their risk-neutral alternatives (θ3 ˆRN and θ4 ):

109     .1873 if c = 0 .1520 if c = 0     ˆRA ˆRA θ3 ≈ .7316 if c = .35 ; θ4 ≈ .3865 if c = .35 ;       1 if c = .85 .1780 if c = .85     .1875 if c = 0 .1523 if c = 0     ˆRN ˆRN θ3 = .7125 if c = .35 ; θ4 ≈ .3798 if c = .35 .       1 if c = .85 0 if c = .85

B.4 Instructions and Screenshots

Instructions for the MIXED treatment are reprinted below. The instructions for NAIVE- MIXED are identical except for the graph depicting the strategies of computer Players 1 and 2. The ORDERED instructions are similar except that the initial instructions describe only the No-Cap setting without discussion of the capacity constraint or waiting cost. After the ﬁrst six rounds of this treatment, subjects recieve additional instructions which explain the capacity constraint and waiting cost, which are present only in rounds 7-18 of this treatment.

This is an experiment in the economics of decision making. If you follow these instructions carefully and make good decisions, you may earn a considerable amount of money which will be paid to you in cash at the end of the experiment. The experiment is divided into 18 rounds. At the beginning of the experiment, you will be randomly assigned a role of either Player 3 or Player 4, and you will keep the same role in every round of the experiment. At the beginning of each round, you will be matched randomly and anonymously with a player of the other role, creating a match between Player 3 and Player 4. The match in each round is determined independently of matches in previous

110 rounds. You and the person with whom you are matched will each make a choice after choices are made by two computer players, Player 1 and Player 2. Each player is asked to choose one of two alternatives, LEFT and RIGHT. Choices are made in sequence: computer Player 1 chooses ﬁrst, then computer Player 2, followed by human Player 3 and ﬁnally human Player 4. Each player receives a private signal, which is a number drawn randomly and uniformly from the interval [0,100], independent of the private signals drawn for the other players. That is, for each player, each number in the interval [0,100] is equally likely to be drawn as that players private signal, regardless of which numbers are drawn for the other players. All players see only their own signal and do not see the signals of any other players. Players 2, 3 and 4 see the choice of the player who chooses immediately before they do, but not the choices of the other players. That is, Player 2 sees the choice of Player 1, Player 3 sees the choice of Player 2, and Player 4 sees the choice of Player 3. Players see the choice of the preceding player (LEFT or RIGHT), but not the private signal of the preceding player. When it is your turn to make a choice, you will see the choice of the preceding player (LEFT or RIGHT) on your computer screen, and you will be asked to enter a critical number between 0 and 100 before your private signal is shown to you. If your private signal turns out to be LESS than this number, your choice will be LEFT, and if your private signal turns out to be GREATER than this number, your choice will be RIGHT. In other words, when you enter this critical number, it means that for each possible private signal greater than this number, you would choose RIGHT, and for each possible private signal less than this number, you would choose LEFT. After you enter this number, your private signal will be drawn and your choice will be made for you according to the number you enter. When the round ends, your private signal will be shown to you along with your chosen alternative.

111 Payoffs for this experiment are denominated in Experimental Currency Units (ECUs). Your net payoff in ECUs in a given round is equal to the gross value of your chosen alternative minus any cost you incur. The gross value of RIGHT in a given round is equal to the average of the private signals drawn for all four players in that round. The gross value of LEFT is equal to 100 minus the average of the private signals drawn for all four players in that round. For example, if the four private signals drawn are 11, 42, 83 and 20 then the average of the signals is (11 + 42 + 83 + 20)/4, which is equal to 39. Hence, the gross value of RIGHT is 39 ECUs and the gross value of LEFT is 61 ECUs (100 39 = 61) in that round. Players 3 and 4 incur a cost if they choose the same alternative as at least two of the preceding players. The cost in each round will be equal to 0, 35 or 85, and the cost is the same for both Players 3 and 4 in any given round. For example, suppose the cost is 35. If both Players 1 and 2 chose the same alternative as Player 3 in that round then 35 ECUs are subtracted from the gross value of Player 3’s chosen alternative to determine her net payoff for the round. Otherwise, Player 3 does not pay the cost. If at least two of Players 1, 2 and 3 chose the same alternative as Player 4 in that round, 35 ECUs are subtracted from the gross value of Player 4s chosen alternative to determine her net payoff for the round. Otherwise, Player 4 does not pay the cost. Players 1 and 2 never incur a cost. The computer players, Player 1 and Player 2, are programmed to choose according to the rules shown in the graph below, which includes Player 1s private signal on the horizontal axis and Player 2s private signal on the vertical axis. The solid line inside the graph represents the rule followed by computer Player 1. If it receives a private signal to the right of this line, it chooses RIGHT, and if it receives a private signal to the left of this line, it chooses LEFT. The dotted line inside the graph represents the rule followed by computer Player 2. If it receives a signal above this line, it chooses RIGHT, and if it receives a signal below this

112 line, it chooses LEFT. The regions of the graph are labeled by the choices Players 1 and 2 make for each pair of Player 1 and Player 2 signals in that region.

The cost will be 0, 35 and 85 for six rounds each and will be known (and the same) for both players, but the order in which these 18 rounds will be played is determined randomly. For each of the three cost levels, one of the six rounds played at that cost will be drawn randomly. You will be paid your earnings for only these three rounds. Because you do not know which rounds will be chosen for payment, you should play each round as if you will be paid for it. At the end of the experiment, you will be paid $0.10 per ECU earned in the three rounds selected for payment plus the starting balance of 50 ECUs. You will also receive the participation fee of $5. Before we begin, we will play two trial rounds that do not count for payment so that you can get familiar with the software. Your role in the trial rounds (Player 3 or Player 4) will be the same as in the rest of the experiment. If you have any questions about the instructions, please ask them now. If you have questions during the experiment, please raise your hand and one of the experimenters will assist you. Please turn oﬀ your cell phones at

113 this point. You should not communicate with any of the other participants for the duration of the experiment.

114 Figure B.1: Player 3 Choice Screen

115 Figure B.2: Player 4 Choice Screen

116 Figure B.3: Player 3 Feedback Screen

117 Figure B.4: Player 4 Feedback Screen

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