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
By
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 phenomena 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 University 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 Associate - The Ohio State University
Publications
Research Publications
Jones, M.T. (2011). Bidding fever in eBay auctions of Amazon.com gift certificates. Economics Letters 113(1), 5-7.
Fields of Study
Major Field: Economics
v
Table of Contents
Page
Abstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
ii
Acknowledgments . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
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Vita . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
v
List of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
viii
List of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
x
1.
1
Strategic Complexity and Cooperation: An Experimental Study . . . . . . . . .
1.1
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1.5
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An Experiment on Herding with Capacity Constraints . . . . . . . . . . . . . .
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2.1
2.2
2.3
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1.6
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2.4
Introduction . . . . . . . . . .
Theoretical Background . . . .
Experimental Design . . . . . .
Research Questions . . . . . . .
Results . . . . . . . . . . . . .
1.5.1 Aggregate Cooperation
1.5.2 Strategy Inference . . .
1.5.3 Regression Analysis . .
Conclusion . . . . . . . . . . .
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Introduction . . . . . . . . . . . .
Related Literature . . . . . . . . .
Model . . . . . . . . . . . . . . . .
2.3.1 Risk-Neutral Bayesian Nash
2.3.2 Bounded Rationality . . . .
Experimental Design . . . . . . . .
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Equilibrium
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2.5
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eBay Auctions of Amazon.com Gift Certificates: A Study of Bidding Fever in the
Field . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
82
3.1
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2.6
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Experimental Questions and Results . . . .
2.5.1 Effects of the Capacity Constraint .
2.5.2 Subjects Satisfying Basic Rationality
2.5.3 Rationality vs. Bounded Rationality
Conclusion . . . . . . . . . . . . . . . . . .
Introduction . . . . . . . .
Data . . . . . . . . . . . . .
Interpretation . . . . . . . .
Alternative Interpretations .
Regression Analysis . . . .
Conclusion . . . . . . . . .
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Appendices
92
A.
Appendix to Strategic Complexity and Cooperation: An Experimental Study . .
92
A.1 Directed Graph Representations of Selected Automaton Strategies
Treatment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
A.2 Instructions and Screenshots . . . . . . . . . . . . . . . . . . . .
A.2.1 Phase I Instructions . . . . . . . . . . . . . . . . . . . . .
A.2.2 Phase II Instructions . . . . . . . . . . . . . . . . . . . . .
92
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97
B.
in Each
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Appendix to An Experiment on Herding with Capacity Constraints . . . . . . . 105
B.1
B.2
B.3
B.4
Derivation of RNBNE . . . . .
Derivation of Level-k Strategies
Risk Aversion . . . . . . . . . .
Instructions and Screenshots .
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105
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109
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 Rationality . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
68
Cost Level in Trial Rounds and Rounds 1-6 of MIXED/ORDERED . . . . .
69
2.5
viii
2.6
ACT and SAT-ACT Concordance Score Summary Statistics . . . . . . . . .
71
2.7
Probits Reporting Marginal Effects of ACT/Major on Satisfying Basic Rationality . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
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 Blonski 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 dominance 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
1
There 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
2
See 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).
3
See 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
4
This 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
5
This 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.
6
Others 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 strategyimplementing 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.
7
Binmore 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
8
Dal 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
, where λ close to zero favors cooperation and
cooperative vs. a selfish strategy for this experiment is λ = 26
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
9
See Appendix A for the instructions given to subjects. The experimental software is programmed in
zTree (Fischbacher, 2007).
10
Notes 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.
11
Each 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.
12
See Figure A.5 in Appendix A.
13
See Figure A.6 in Appendix A.
14
See 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
15
See 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
16
Subjects 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.
17
In 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.
18
The 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.
19
The 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.
20
I 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
21
The 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
Phase
I
NOSWITCH
40.6%
SWITCH-C
35.3%
SWITCH-D
29.5%***
36.6%
NOSWITCH-R
<<<
<<<
1st Stage
II
I
40.2%
55.5%
34.5%
41.6%**
33.7%*** 42.4%***
57.8%*** 43.4%**
<<<
II
60.0%
50.6%
46.8%***
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 SWITCHC.23 I find that subjects are less likely to adopt a cooperative strategy in SWITCH-C than in
22
It 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.
23
See 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
24
See 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 NOSWITCHR, 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
25
A 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).
26
See 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.
27
The 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
Always Cooperate
Tit-for-Tat
Tit-for-2-Tats
Tit-for-3-Tats
2-Tits-for-1-Tat
2-Tits-for-2-Tats
2-Stage Trigger
Grim Trigger
Forgiving Trigger
Twice-Forgiving Trigger
Win-Stay Lose-Shift
2-Stage Win-Stay Lose-Shift
Always Defect
Cooperate-Defect
Selfish TFT
Selfish TF2T
Selfish TF3T
Selfish GT
Selfish FT
Alternate
Abbreviation
AC
TFT
TF2T
TF3T
2TFT
2TF2T
T2
GT
FT
2FT
WSLS
WSLS2
AD
CD
STFT
STF2T
STF3T
SGT
SFT
ALT
Description
Cooperate in every stage.
Cooperate unless opponent defected in last stage.
Cooperate unless opponent defected in both of last 2 stages.
Cooperate unless opponent defected in all of last 3 stages.
Cooperate unless opponent defected in either of last 2 stages.
Cooperate unless opponent defected twice consecutively in 2 of last 3 stages.
Cooperate until opponent defects, then defect for 2 stages.
Cooperate until opponent defects, then defect forever.
Cooperate until opponent defects in 2 consecutive stages, then defect forever.
Cooperate until opponent defects in 3 consecutive stages, then defect forever.
Cooperate if both players chose same action in last stage, otherwise defect.
Cooperate if both players chose same action in last 2 stages, otherwise defect.
Defect in every stage.
Cooperate in stage 1, then defect forever.
Defect in stage 1, then play TFT.
Defect in stage 1, then play TF2T.
Defect in stage 1, then play TF3T.
Defect in stage 1, then play GT.
Defect in stage 1, then play FT.
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
if the indicator function yirt (sk ) = 1{sirt (sk ) + γirt ≥ 0} takes a value of 1 and defects
otherwise, where sirt (sk ) is the action prescribed by strategy sk (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
YY
1
1
form pi (sk ) =
(
)yirt (
)1−yirt . The resulting logk
k )/γ)
1
+
exp(−s
(s
)/γ)
1
+
exp(s
(s
irt
irt
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
28
Results 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
Phase
AC
TFT
TF2T
TF3T
2TFT
2TF2T
T2
GT
FT
2FT
WSLS
WSLS2
AD
CD
STFT
STF2T
STF3T
SGT
SFT
ALT
NOSWITCH
I
II
0.03
0
(0.03)
(0)
0.08
0.16*
(0.07)
(0.09)
0
0.05
(0)
(0.05)
0
0.06
(0.02)
(0.04)
0
0.14
(0)
(0.13)
0.04
0
(0.06)
(0.06)
0
0.04
(0)
(0.03)
0.24**
0.14
(0.10)
(0.11)
0.09
0
(0.08)
(0.01)
0
0
(0.02)
(0.01)
0.02
0
(0.05)
(0)
0
0.02
(0)
(0.02)
0.26*** 0.29***
(0.08)
(0.07)
0.06
0.03
(0.05)
(0.03)
0.18**
0.04
(0.07)
(0.03)
0
0
(0.03)
(0)
0
0
(0)
(0)
0
0.03
(0.02)
(0.02)
0
0
(0)
(0)
0
0
(0)
(0)
SWITCH-C
I
II
0
0.03
(0)
(0.03)
0.08
0.11*
(0.07)
(0.06)
0
0.11*
(0.01)
(0.06)
0
0
(0)
(0.02)
0.05
0
(0.07)
(0.01)
0
0
(0.05)
(0.02)
0
0
(0)
(0)
0.10*
0.18*
(0.06)
(0.09)
0.11
0
(0.07)
(0.03)
0.04
0.01
(0.04)
(0.02)
0
0
(0)
(0)
0
0
(0)
(0)
0.42** 0.45***
(0.16)
(0.09)
0
0.05
(0)
(0.05)
0.07
0.06
(0.07)
(0.04)
0.09
0
(0.08)
(0)
0
0
(0.01)
(0)
0.04
0
(0.06)
(0)
0
0
(0)
(0)
0
0
(0)
(0)
SWITCH-D
I
II
0
0.03
(0)
(0.03)
0.18
0.22***
(0.12)
(0.08)
0
0.10*
(0.01)
(0.06)
0
0
(0.02)
(0)
0
0.06
(0.03)
(0.05)
0.04
0
(0.03)
(0)
0
0
(0)
(0)
0.07
0.04
(0.06)
(0.06)
0.04
0
(0.03)
(0)
0.03
0
(0.02)
(0)
0
0
(0)
(0)
0
0.02
(0)
(0.03)
0.48*** 0.47***
(0.09)
(0.08)
0.03
0
(0.03)
(0)
0.13*
0.06
(0.07)
(0.04)
0
0
(0)
(0.01)
0
0
(0)
(0)
0
0
(0)
(0.01)
0
0
(0)
(0)
0
0
(0)
(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
NOSWITCH-R
I
II
0.06
0
(0.06)
(0)
0.23*
0.39***
(0.14)
(0.11)
0.04
0.13
(0.04)
(0.12)
0.02
0.03
(0.02)
(0.03)
0
0
(0)
(0.04)
0.02
0.04
(0.03)
(0.09)
0
0
(0)
(0)
0.05
0.07
(0.05)
(0.08)
0
0
(0)
(0.02)
0.02
0
(0.01)
(0.02)
0
0
(0)
(0)
0
0
(0)
(0)
0.43*** 0.18***
(0.12)
(0.06)
0.05
0
(0.04)
(0)
0.10
0.11*
(0.11)
(0.06)
0
0
(0)
(0)
0
0
(0)
(0.02)
0
0.03
(0.01)
(0.03)
0
0.03
(0)
(0.02)
0
0
(0.01)
(0)
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 Defect 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
29
Specifically, 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.
30
One-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
31
Given 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%
32
Interestingly, 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.
33
In contrast, Hauk and Nagel (2001) and Hauk (2003) find that subjects mix between different types of
strategies in simultaneous games.
34
I 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.
35
According 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).
36
Data 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
Dependent Variable: Cooperation in —
SWITCH-C
SWITCH-D
Cooperated in First Stage of Previous Rd.
Opponent Cooperated in First Stage of Previous Rd.
# of Stages in Previous Rd.
Cooperated in First Stage of Rd. 1
Opponent Cooperated in First Stage of Rd. 1
Observations
1st Stage, Rounds 2-7
Coefficient Std. Err.
-0.088
(0.059)
-0.122*
(0.069)
0.496***
(0.050)
0.135***
(0.046)
0.019**
(0.008)
0.245***
(0.056)
0.022
(0.056)
612
Any Stage, Rounds 2-7
Coefficient Std. Err.
0.001
(0.050)
-0.080
(0.050)
0.270***
(0.040)
0.058*
(0.034)
0.018***
(0.005)
0.099**
(0.043)
-0.037
(0.040)
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 SWITCHD 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
37
Benjamin 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.
38
See 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
Subjects
34
28
Median
Mean
27.97
0.719
Std. Err.
61.8%
with ACT
SAT Only*
35.3%
2.9%
No Score
Top 5%
23.5%
<Top 20%
14.7%
SWITCH-C
34
28
27.87
0.575
55.9%
35.3%
8.8%
14.7%
14.7%
SWITCH-D
34
27
27.63
0.585
64.7%
29.4%
5.9%
17.6%
17.6%
NOSWITCH-R POOLED
34
136
27
27
27.41
27.72
0.650
0.319
76.5%
64.7%
17.6%
29.4%
5.9%
5.9%
17.6%
18.4%
23.5%
17.6%
*SAT-ACT concordance scores are used for these subjects.
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)
-0.161
(0.164)
-0.202**
(0.080)
<Top 20%
Phase II
0.055
(0.102)
0.001
(0.041)
-0.010
(0.123)
-0.058
(0.084)
Phase II*Top 5%
-0.014
(0.172)
0.065
(0.065)
Phase II*<Top 20%
Observations
1190
4488
SWITCH-C
Top 5%
0.125
(0.130)
0.022
(0.097)
<Top 20%
-0.239
(0.168)
0.054
(0.145)
0.103
(0.072)
0.013
(0.036)
Phase II
Phase II*Top 5%
-0.054
(0.097)
-0.019
(0.049)
Phase II*<Top 20%
0.028
(0.129)
-0.079
(0.073)
Observations
1190
4488
SWITCH-D
Top 5%
0.227
(0.154)
0.050
(0.134)
-0.013
(0.243)
-0.076
(0.104)
<Top 20%
Phase II
0.038
(0.086)
0.038
(0.039)
0.111
(0.114)
0.054
(0.076)
Phase II*Top 5%
-0.162
(0.174)
-0.027
(0.100)
Phase II*<Top 20%
Observations
1190
4488
NOSWITCH-R
Top 5%
0.027
(0.113)
0.025
(0.104)
<Top 20%
-0.350***
(0.082)
-0.081
(0.087)
Phase II
0.281***
(0.044)
0.257***
(0.054)
Phase II*Top 5%
-0.112
(0.118)
-0.054
(0.065)
Phase II*<Top 20%
-0.231*
(0.118)
-0.105
(0.066)
Observations
1190
4488
Controls for no score included, but coeffs. not reported due to the small number of subjects with no score.
Standard errors clustered at the subject level.
*** significant at .01 level; ** significant at .05 level; * significant at .1 level.
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 NOSWITCHR 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)
-0.161
(0.156)
-0.198**
(0.078)
<Top 20%
Phase II
0.056
(0.103)
0.001
(0.040)
-0.010
(0.125)
-0.056
(0.080)
Phase II*Top 5%
Phase II*<Top 20%
-0.015
(0.175)
0.064
(0.063)
SWITCH-C
-0.009
(0.122)
-0.027
(0.073)
SWITCH-C*Top 5%
-0.194
(0.182)
-0.161
(0.105)
SWITCH-C*<Top 20%
-0.070
(0.245)
0.275
(0.170)
0.048
(0.125)
0.012
(0.055)
SWITCH-C*Phase II*
SWITCH-C*Phase II*Top 5%
-0.044
(0.157)
0.038
(0.100)
0.023
(0.229)
-0.134
(0.085)
SWITCH-C*Phase II*<Top 20%
SWITCH-D
-0.095
(0.131)
-0.081
(0.079)
SWITCH-D*Top 5%
-0.095
(0.217)
-0.138
(0.135)
0.157
(0.270)
0.134
(0.154)
SWITCH-D*<Top 20%
SWITCH-D*Phase II
-0.018
(0.134)
0.039
(0.059)
SWITCH-D*Phase II*Top 5%
0.120
(0.162)
0.117
(0.119)
-0.165
(0.234)
-0.087
(0.112)
SWITCH-D*Phase II*<Top 20%
NOSWITCH-R
0.006
(0.115)
-0.019
(0.074)
NOSWITCH-R*Top 5%
-0.277
(0.151)
-0.161
(0.106)
-0.217
(0.168)
0.137
(0.131)
NOSWITCH-R*<Top 20%
NOSWITCH-R*Phase II
0.223**
(0.098)
0.255***
(0.067)
-0.104
(0.171)
0.004
(0.106)
NOSWITCH-R*Phase II*Top 5%
NOSWITCH-R*Phase II*<Top 20%
-0.224
(0.192)
-0.152
(0.073)
Observations
4760
17952
Controls for no score included; coeffs. not reported due to small # of subjects with no score.
Standard errors clustered at the subject level.
*** significant at .01 level; ** significant at .05 level; * significant at .1 level.
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
39
See 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
40
See 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
41
See Weizsacker (2010) for a review of these findings.
42
in equilibrium. This result emerges in both the standard binary-signal environment (see Anderson 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
42
A 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 highinformed individuals and find that low-informed individuals behave consistently with Quantal 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 overconfident 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
43
Another 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
to
P4
i=1 θi
4
, while the quality of option L is equal to 1 −
P4
i=1 θi
4
. Each option has a capacity
44
See Smith and Sorensen (2000), Celen and Kariv (2004a, 2004b, 2005) and Owens (2011)
45
See 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:
E[U (
P4
i=1 θi
4
≥ E[U (1 −
− Cn (x1 , ..., xn−1 , R))|θn , xn−1 = R]
P4
i=1 θi
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:
xn (xn−1 = R) =



R if θn ≥ θ̂n


L
.
if θn < θ̂n
The problem is symmetric for xn−1 = L, so in this case player n follows a decision rule given
by:
xn (xn−1 = L) =



R if θn ≥ 1 − θ̂n


L
.
if θn < 1 − θ̂n
Therefore, the equilibrium is fully characterized by θ̂n as a function of c for each n. I refer
to θ̂n as player n’s equilibrium strategy at waiting cost c.
47
2.3.1
Risk-Neutral Bayesian Nash Equilibrium
The Risk-Neutral Bayesian Nash Equilibrium (RNBNE) strategies, θ̂n , for the four players
are:
1
θ̂1 = ,
2
1
θ̂2 = ,
4
θ̂3 =



 3+24c
16


1
if c ≤
13
24
if c >
13
24
,
θ̂4 =



1

(39 + 368c − 576c2 ) if c ≤

256



13
24
if c ∈ ( 13
, 13 ] .
24 16
13−16c
16






0
if c >
13
16
Derivation of the RNBNE is relegated to Appendix B.46 The RNBNE strategies for Players
3 and 4 (P3 and P4), θ̂3 and θ̂4 , are shown as a function of the waiting cost, c, in Figure 2.1.
For low waiting costs (c <
5
),
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
, 24 )), the incentive to
P2 shrinks as the waiting cost increases. For moderate costs (c ∈ [ 24
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
as the cost increases. When the waiting cost is sufficiently large (c ≥
13
),
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
46
In 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
the cost when it reaches c =
23
.
72
The range of signals for which P4 follows P3 continues to
increase with the cost until it reaches c ≥
13
,
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
47
As 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.
48
See 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
49
This 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 (θ̃2 = 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.
50
See 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
51
Two 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
52
Kolmogorov-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 NAIVEMIXED 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
Treatment
No-Cap
Mean
=0
=100
MIXED
ORDERED
NAIVE-MIXED
45.2
50.4
42.3
16.1%
11.9%
20.7%
MIXED
ORDERED
NAIVE-MIXED
52.2
43.8
51.0
15.0%
9.5%
8.0%
Low-Cost
High-Cost
Mean
=0
=100 Mean
=0
=100
Player 3
10.6% 66.4
2.8% 21.1% 70.5
2.2% 30.6%
8.3%
59.6
8.3% 16.1% 76.3
2.4% 38.1%
8.0%
69.3
3.3% 25.3% 77.8
1.3% 36.0%
Player 4
13.9% 49.6 18.9% 12.2% 45.9 17.2% 14.4%
4.2%
52.4 10.7% 10.1% 52.3 14.9% 14.3%
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 signedranks 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
53
Because 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.
54
For 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
55
See the results of Celen and Kariv (2004, 2005) for direct comparisons or the survey of Weizsacker (2010)
for more general findings.
56
This 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
Treatment
No-Cap
Low-Cost
MIXED
ORDERED
NAIVE-MIXED
18.8
18.8
25.0
71.3
71.3
60.0
MIXED
ORDERED
NAIVE-MIXED
15.2
15.2
18.8
38.0
38.0
59.0
Mean Strategies
High-Cost
No-Cap
Player 3
100.0
45.2
100.0
50.4
100.0
42.3
Player 4
0.0
52.2
0.0
43.8
75.0
51.0
<<<
<
<<<
<
Low-Cost
High-Cost
66.4
59.6
69.3
70.5
76.3
77.8
<<<
<<
49.6
52.4
57.8
45.9
52.3
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
57
Treatment 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 underreliance on private information.
58
It 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
Treatment
MIXED
ORDERED
NAIVE-MIXED
Player 3
Setting
RNBNE First
No-Cap
18.8
50.4
Low-Cost
71.3
64.2
High-Cost
100.0
56.9
No-Cap
18.8
54.6
Low-Cost
71.3
61.1
High-Cost
100.0
67.1
No-Cap
25.0
48.8
Low-Cost
60.0
61.8
High-Cost
100.0
73.2
Player 4
Last RNBNE First
39.8
15.2
60.8
71.3
38.7
56.1
78.0
0.0
48.6
45.6
15.2
44.3
56.5
38.7
40.4
82.1
0.0
63.9
50.1
18.8
53.8
78.0
59.0
56.5
78.7
75.0
60.8
Last
46.0
45.5
40.1
46.5
63.1
47.5
55.2
60.5
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 incorporate 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
59
For comparison, Celen and Kariv (2005) report that 60.8% of strategies in their experiment satisfy the
basic rationality condition.
60
Treatment 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
Treatment
No-Cap
Low-Cost
MIXED
ORDERED
NAIVE-MIXED
18.8
18.8
25.0
71.3
71.3
60.0
MIXED
ORDERED
NAIVE-MIXED
15.2
15.2
18.8
38.0
38.0
59.0
Mean Strategies
High-Cost
No-Cap
Player 3
100.0
26.9
100.0
37.6*
100.0
27.0
Player 4
0.0
32.9
0.0
33.0
75.0
41.8*
Low-Cost
<<<
<<
<<<
<<
<<
63.6
56.6
73.4
29.6
50.0**
53.8**
High-Cost
<<<
70.4
82.9
84.1
<<
33.0
50.5
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
MIXED
1
0
2
85
MIXED
MIXED
3
35
ORDERED Pooled 0
T2 1
35 35
35 0
35 85
0
0
2 3 4 5
85 0 85 0
0 35 35 0
35 0 85 85
0 0 0 0
6
85
35
85
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 indicators 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
61
See 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
Mean
Std. Err.
with ACT
with SAT Only*
with No Score
in Top 5%
below Top 20%
27
27.58
0.289
66.9%
20.5%
12.7%
18.7%
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
62
Probit 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.
63
This 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
Variable
Score in Top 5%
Score below Top 20%
No Score Reported
Quantitative Major
Observations
Player 3
Estimate (S.E.)
0.236
(0.137)
0.078
(0.136)
0.357**
(0.130)
0.016
(0.153)
83
Player 4
Estimate (S.E.)
0.263*
(0.129)
-0.024
(0.142)
0.123
(0.169)
0.071
(0.149)
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?
64
This result is consistent with the findings of Ivanov et al.(2009, 2010) that subjects in their endogenoustiming 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
65
Due 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 HighCost 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
(MSD≤1000)
RNBNE
L1
L2
Low-Cost
RNBNE L1
2
4
10
4
1
1
Min. MSD
L2 MSD>1000
1
6
10
1
2
2
Total
13
25
6
Table 2.9: Transition Matrix Showing Player 4 Best-Fitting Theory Across Settings
No-Cap Min. MSD
(MSD≤1000)
RNBNE
L1
L2
Low-Cost
RNBNE L1
0
0
8
7
6
1
Min. MSD
L2 MSD>1000
0
3
11
8
1
2
High-Cost Min. MSD
RNBNE L1 L2 MSD>1000
1
0
0
2
7
4
9
14
4
0
1
5
Total
3
34
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. Because 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
Variable
Score in Top 5%
Score below Top 20%
No Score Reported
Quantitative Major
Constant
Observations
Score in Top 5%
Score below Top 20%
No Score Reported
Quantitative Major
Constant
Observations
MSD-RNBNE
MSD-L1
Estimate (S.E.) Estimate (S.E.)
Player 3
-185.2
(282.2) -259.5
(305.2)
206.6
(253.5) 198.3
(274.2)
-75.5
(326.7) 85.7
(353.3)
-520.1*
(271.5) -725.9**
(293.6)
1707.3*** (153.1) 1632.0*** (165.6)
83
83
Player 4
-801.7**
(394.4) 746.9*
(440.8)
-557.1
(376.7) -15.7
(421.1)
-586.5
(472.8) -236.4
(528.5)
166.5
(398.5) 234.1
(445.4)
2610.9*** (220.7) 2250.2*** (246.7)
83
83
MSD-L2.
Estimate (S.E.)
-168.7
144.6
-39.5
-461.1*
1616.5***
83
(263.6)
(236.8)
(305.1)
(253.5)
(143.0)
216.2
-132.3
-334.8
152.6
1734.3***
83
(278.1)
(265.6)
(333.3)
(280.9)
(155.6)
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
Mean
$58.04
$25.00
Median
Max
$573.45
$5.00
Min
3.2
Price Paid by Winner
$56.92
$25.31
$559.24
$4.25
# of Bids
7.4
6.0
50
1
Winner’s Bidder Rating
780
60
20453
0
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
66
The 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.
67
Buy-it-now and best-offer sales are excluded from the sample.
83
Table 3.2: Summary of Overbidding
Overbid
Overbid
Overbid
Overbid
Overbid
by
by
by
by
# (out of 506 obs.)
208
74
>$1
>$5
27
71
>5%
51
>10%
% of obs.
41.1%
14.6%
5.3%
14.0%
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
68
Categories in Table 3.2 are not mutually exclusive.
84
Table 3.3: Overbidding by Time and Day of Week
4am-12pm ET
12pm-8pm ET
8pm-4am ET
Monday
Tuesday
Wednesday
Thursday
Friday
Saturday
Sunday
Auctions
155
265
86
77
82
50
51
75
75
96
Overbid
61
113
34
29
29
24
21
36
33
36
% Overbid
39.4%
42.6%
39.5%
37.7%
35.4%
48.0%
41.2%
48.0%
44.0%
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
0-9
10-29
30-129
130-499
500+
Total
Auctions
98
88
85
96
110
477
Overbid
54
44
35
37
26
196
% Overbid
55.1%
50.0%
41.2%
38.5%
23.6%
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).
69
Some 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
Variable
bids
lograting
face
disc*fd
date
aft
eve
latewk
constant
Observations
w/ Bidder Rating
Estimate
(Std. Err.)
0.263***
(0.092)
-0.708***
(0.165)
-0.083***
(0.029)
0.076**
(0.031)
-0.002
(0.024)
2.174**
(0.915)
-0.427
(1.205)
1.874**
(0.801)
1.405
(1.426)
477
w/o Bidder Rating
Estimate
(Std. Err.)
0.293***
(0.091)
—
—
-0.074***
(0.028)
0.068**
(0.031)
-0.017
(0.024)
2.228**
(0.911)
-0.214
(1.208)
1.880**
(0.799)
-1.797
(1.219)
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
70
Though 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 documented 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 Strategies 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 NOSWITCHR 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:
E[
P4
i=1 θi
4
≥ E[1 −
− Cn (x1 , ..., xn−1 , R)|θn , xn−1 = R]
P4
i=1 θi
4
− Cn (x1 , ..., xn−1 , L)|θn , xn−1 = R].
Because θn+1 , ..., θ4 are independent with mean 21 , this inequality can be re-written as,
E[
Pn−1
θi +θn + 12 (4−n)
− Cn (x1 , ..., xn−1 , R)|θn , xn−1 = R]
4
Pn−1
θ +θ + 1 (4−n)
− Cn (x1 , ..., xn−1 , L)|θn , xn−1
− i=1 i 4n 2
i=1
≥ E[1
= R],
which simplifies to:
n−1
X
n
θn ≥ − E[
θi − 2(Cn (x1 , ..., xn−1 , R) − Cn (x1 , ..., xn−1 , L))|xn−1 = R].
2
i=1
Hence, player n uses a cutoff strategy given by:
xn (xn−1 = R) =



R if θn ≥ θ̂n


L
105
if θn < θ̂n
,
where θ̂n =
n
2
− E[
Pn−1
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:
xn (xn−1 = L) =



R if θn ≥ 1 − θ̂n


L
.
if θn < 1 − θ̂n
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
follows trivially that θ̂1 =
1
2
holds.
Player 2: Because neither option’s capacity can be reached after only one player’s choice,
E[θ1 − 2(C2 (x1 , R) − C2 (x1 , L))|x1 = R] = E[θ1 |x1 = R] =
θ̂2 = 1 −
3
4
=
1
4
3
4
holds, which imples that
holds.
Player 3: By Bayes’ Rule it follows from θ̂1 and θ̂2 that P r(x1 = R|x2 = R) =
Hence, E[θ1 + θ2 |x2 = R] =
3 5
(
4 8
+ 68 ) + 14 ( 78 + 28 ) =
21
16
3
E[θ1
4
3
4
holds.
+ θ2 |x1 = x2 = R] + 41 E[θ1 + θ2 |x1 = L, x2 = R] =
holds. Also, E[2(C3 (x1 , R) − C3 (x1 , L))|x2 = R] = 2 43 c =
21
Therefore, θ̂3 is equal to the minimum of 32 − 16
+ 6c
=
4
3+24c
16
that it is never optimal for Player 3 to follow Player 2.
and 1 because
3+24c
16
3+24c
16
6c
4
holds.
> 1 implies
> 1 holds if and only if c >
13
24
holds.
Player 4: By Bayes’ Rule it follows from θ̂1 ,θ̂2 and θ̂3 that if c ≤
R|x3 = R) =
13−24c
16
13
24
holds then P r(x2 =
holds. Hence, we have,
E[θ1 + θ2 + θ3 |x3 = R]
=
13−24c 3
( 4 E[θ1
16
+ θ2 + θ3 |x1 = x2 = x3 = R] + 14 E[θ1 + θ2 + θ3 |x1 = L, x2 = x3 = R]) ,
+ 3+24c
( 14 E[θ1 + θ2 + θ3 |x1 = x3 = R, x2 = L] + 43 E[θ1 + θ2 + θ3 |x1 = x2 = L, x3 = R])
16
where the following hold if c ≤
13
24
holds:
106
E[θ1 + θ2 + θ3 |x1 = x2 = x3 = R] =
5
8
+ 68 +
19+24c
;
32
E[θ1 + θ2 + θ3 |x1 = L, x2 = x3 = R] =
7
8
+ 28 +
19+24c
;
32
E[θ1 + θ2 + θ3 |x1 = x3 = R, x2 = L] =
1
8
+ 68 +
29−24c
;
32
E[θ1 + θ2 + θ3 |x1 = x2 = L, x3 = R] =
3
8
+ 28 +
29−24c
.
32
473−576c2
.
256
Some algebra yields E[θ1 +θ2 +θ3 |x3 = R] =
C4 (x1 , x2 , L))|x3 = R] = 2( 13−24c
c+
16
holds then we have θ̂4 = 2 −
473−576c2
256
1 3+24c
c
4 16
+
−
In addition, we have E[2(C4 (x1 , x2 , R)−
3 3+24c
c)
4 16
368c−1152c2
256
=
=
368c−1152c2
.
256
39+368c−576c2
.
256
Therefore, if c ≤
However, if c >
13
24
13
24
holds,
then we have instead:
P r(x2 = R|x3 = R) = 0;
E[θ1 + θ2 + θ3 |x1 = x3 = R, x2 = L] =
1
8
+ 68 + 12 ;
E[θ1 + θ2 + θ3 |x1 = x2 = L, x3 = R] =
3
8
+ 28 + 12 .
In this case, E[θ1 + θ2 + θ3 |x3 = R] =
19
16
2( 41 c − 34 c) = −c. Therefore, if c >
holds then θ̂4 is equal to the maximum of 2 −
c =
13−16c
16
13−16c
16
and 0 because
13−16c
16
13
24
and E[2(C4 (x1 , x2 , R) − C4 (x1 , x2 , L))|x3 = R] =
19
16
−
< 0 implies that Player 4 should always follow Player 3.
< 0 holds if and only if c >
13
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
given x3 = R, E[
P4
i=1 θi
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
The Level-k strategies of Players 3 and 4 are denoted by θ̃3Lk and θ̃4Lk . The Level-1 Player
n believes that P r(xn−2 = R|xn−1 = R) =
1
2
and E[θi |xi ] =
107
1
2
hold for all i < n. For Player
3, E[2(C3 (x1 , R) − C3 (x1 , L))|x2 = R] = 2 12 c = c holds. Hence, θ̃3L1 is equal to the minimum
of
3
2
−1+c =
1+2c
2
and 1 because
1+2c
2
> 1 implies that it is never optimal for Player 3 to
follow Player 2. For Player 4, E[2(C4 (x1 , x2 , R) − C4 (x1 , x2 , L))|x3 = R] = 2( 43 c − 14 c) = c
holds. Hence, θ̃4L1 is equal to the minimum of 2 − 32 + c =
1+2c
2
and 1 because
1+2c
2
that it is never optimal for Player 4 to follow Player 3.
1+2c
2
> 1 holds if and only if c >
> 1 implies
1
2
holds.
The Level-2 Player 3 believes that P r(x1 = R|x2 = R) = 21 , E[θ1 |x2 ] = 21 , E[θ2 |x2 =
3
4
R] =
1
4
and and E[θ2 |x2 = L] =
hold. It follows that E[2(C3 (x1 , R) − C3 (x1 , L))|x2 = R] =
2 21 c = c holds. Therefore, θ̃3L2 is equal to the minimum of
1+4c
4
3
2
−
5
4
1+4c
4
+c =
> 1 implies that it is never optimal for Player 3 to follow Player 2.
and only if c >
3
4
and 1 because
1+4c
4
> 1 holds if
holds.
The Level-2 Player 4 believes that P r(x1 = R|x2 = R) = 12 , E[θ1 |x2 ] = 21 , E[θ2 |x2 =
R] =
3
4
1
4
and E[θ2 |x2 = L] =
hold and that Player 3’s strategy is her Level-1 strategy.
1
2
By Bayes’ Rule it follows that if c <
and if c ≥
1
2
holds then we have P r(x2 = R|x3 = R) =
1
2
holds then we have P r(x2 = R|x3 = R) = 0. Hence, if c <
we have E[θ1 + θ2 + θ3 |x3 = R] =
θ3 |x2 = L, x3 = R] =
1−2c
(2
2
+ 2c ) +
1−2c
E[θ1
2
1+2c 3
(2
2
+ θ2 + θ3 |x2 = x3 = R] +
− 2c ) =
have E[θ1 + θ2 + θ3 |x3 = R] = 54 . Also, if c <
C4 (x1 , x2 , L))|x3 = R] = 2( 1−2c
c+
2
1 1+2c
c
2 2
−
1
2
7−2c−4c2
,
4
and if c ≥
holds then
1+2c
E[θ1
2
1
2
1−2c
,
2
+ θ2 +
holds then we
holds then we have E[2(C4 (x1 , x2 , R) −
1 1+2c
c)
2 2
= c − 2c2 , and if c ≥
1
2
holds then we
have E[2(C4 (x1 , x2 , R) − C4 (x1 , x2 , L))|x3 = R] = 2( 12 c − 21 c) = 0. Therefore, θ̃4L2 is equal to
2−
7−2c−4c2
4
+ c − 2c2 =
1+6c−4c2
4
if c <
1
2
holds and θ̃4L2 is equal to 2 −
5
4
=
3
4
if c ≥
1
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’
Rule it follows that if c <
c ≥
3
4
3
4
holds then we have P r(x2 = R|x3 = R) =
holds then we have P r(x2 = R|x3 = R) = 0. Hence, if c <
E[θ1 +θ2 +θ3 |x3 = R] =
3−4c
E[θ1 +θ2 +θ3 |x2
4
3
4
3−4c
,
4
and if
holds then we have
= x3 = R]+ 1+4c
E[θ1 +θ2 +θ3 |x2 = L, x3 = R] =
4
108
3−4c 3 5
( 4 ( 8 + 68 + 58 + 2c )+ 41 ( 78 + 82 + 85 + 2c ))+ 1+4c
( 14 ( 18 + 68 + 87 − 2c )+ 34 ( 38 + 28 + 78 − 2c ))
4
4
and if c ≥
3
4
holds then we have E[θ1 + θ2 + θ3 |x3 = R] = 45 . Also, if c <
have E[2(C4 (x1 , x2 , R) − C4 (x1 , x2 , L))|x3 = R] = 2( 3−4c
c+
4
if c ≥
3
4
1 1+4c
c
4 4
−
=
3
4
3 1+4c
c)
4 4
236−16c−128c2
,
128
holds then we
=
5c−12c2
,
4
and
holds then we have E[2(C4 (x1 , x2 , R) − C4 (x1 , x2 , L))|x3 = R] = 2( 21 c − 12 c) = 0.
Therefore, θ̃4L3 is equal to 2 −
equal to 2 −
5
4
=
3
4
if c ≥
3
4
236−16c−128c2
128
+
5c−12c2
4
=
20+176c−256c2
128
if c <
3
4
holds and θ̃4L3 is
holds.
In NAIVE-MIXED, the Level-3 Player 4 believes that P r(x1 = R|x2 = R) = 21 , E[θ1 |x2 ] =
1
,
2
E[θ2 |x2 = R] =
3
4
and E[θ2 |x2 = L] =
1
4
hold and that Player 3’s strategy is her
Level-2 strategy. By Bayes’ Rule it follows that if c <
R|x3 = R) =
if c <
3
4
3−4c
,
4
and if c ≥
3
4
R] + 1+4c
E[θ1 + θ2 + θ3 |x2 = L, x3 = R] =
4
3
4
holds then we have P r(x2 =
holds then we have P r(x2 = R|x3 = R) = 0. Hence,
holds then we have E[θ1 + θ2 + θ3 |x3 = R] =
and if c ≥
3
4
3−4c 1
(2
4
3−4c
E[θ1
4
+ θ2 + θ3 |x2 = x3 =
+ 34 + 85 + 2c ) + 1+4c
( 12 + 41 + 78 − 2c ) =
4
holds then we have E[θ1 + θ2 + θ3 |x3 = R] = 54 . Also, if c <
c, and if c ≥
we have E[2(C4 (x1 , x2 , R) − C4 (x1 , x2 , L))|x3 = R] = 2( 3−4c
4
3
4
3
4
58−32c2
,
32
holds then
holds then we
have E[2(C4 (x1 , x2 , R) − C4 (x1 , x2 , L))|x3 = R] = 2( 12 c − 21 c) = 0. Therefore, θ̃4L3 is equal to
2
+ 2( 3−4c
c=
2 − 58−32c
32
4
B.3
6+486c−32c2
32
if c <
3
4
holds and θ̃4L3 is equal to 2 − 54 =
3
4
if c ≥
3
4
holds.
Risk Aversion
I explore the impact of risk-aversion on the Bayesian Nash Equilibrium by solving numerically 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
denoted by θ̂3RA and θ̂4RA and shown below along with their risk-neutral alternatives (θ̂3RN
and θ̂4RN ):
109
θ̂3RA ≈
θ̂3RN
B.4




.1873 if c = 0




θ̂4RA ≈
.7316 if c = .35 ;






1
if c = .85




.1875 if c = 0




= .7125 if c = .35 ;






1
if c = .85
θ̂4RN




.1520 if c = 0




.3865 if c = .35 ;






.1780 if c = .85




.1523 if c = 0




≈ .3798 if c = .35 .






0
if c = .85
Instructions and Screenshots
Instructions for the MIXED treatment are reprinted below. The instructions for NAIVEMIXED 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
118
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