# Testing Models of Strategic Uncertainty:
Equilibrium Selection in Repeated Games

Emanuel Vespa  ,  Taylor Weidman  and  Alistair Wilson

(Date: January, 2021)

###### Abstract.

In repeated-game applications where both the collusive and non-collusive
outcomes can be supported as equilibria, researchers must resolve underlying
selection questions if theory will be used to understand counterfactual
policies. One guide to selection, based on clear theoretical underpinnings,
has shown promise in predicting when collusive outcomes will emerge in
controlled repeated-game experiments. In this paper we both expand upon and
experimentally test this model of selection, and its underlying mechanism:
strategic uncertainty. Adding an additional source of strategic uncertainty
(the number of players) to the more-standard payoff sources, we stress test
the model. Our results affirm the model as a tool for predicting when tacit
collusion is likely/unlikely to be successful. Extending the analysis, we
corroborate the mechanism of the model. When we remove strategic uncertainty
through an explicit coordination device, the model no longer predicts the
selected equilibrium.

We would like to thank: David Cooper, Guillaume Fréchette, Daniella Puzzello
and Lise Vesterlund. This research was funded with support from the National
Science Foundation (SES:1629193).

##  1\. Introduction

Assumptions about which of the possible equilibria best captures the
participants’ economic behavior take on a central role in applications with
repeated interaction. For example, in models of oligopoly where firms interact
repeatedly both collusive and non-collusive equilibria can arise. Researchers
must often find evidence in the data to identify which equilibrium best
captures the status quo. But equilibrium-selection problems persist when
trying to predict counterfactual behavior, where appeals to the data are not
possible. Consider a market where the researcher can establish that the
current behavior of firms matches the non-cooperative equilibrium, but where
their goal is to predict the effect from industry consolidation on consumer
welfare. Embedded within the question is a concern on whether the selected
equilibrium remains the same or will move under the counterfactual. Were a
change isolated solely to the number of firms in the market, a directional
comparative-static on selection could be posited: With fewer firms in the
market, ceteris paribus, the equilibrium is likely to be pushed toward greater
collusion.

But counterfactual analyses are often more involved than a simple comparative
static. In our oligopoly example, while a lower number of firms might push
behavior in the collusive direction, consolidation tends to be accompanied by
other concurrent changes. For example, bigger firms can generate efficiency
gains, increasing the marginal returns to price competition and product
innovation. These accompanying shifts to the profit functions could plausibly
pull more towards the non-collusive equilibria.111The industry-consolidation
literature provides ample evidence that mergers are regularly accompanied by
other changes in addition to a lower number of market participants. For
instance, accompanying effects include lower costs (Farrell and Shapiro,
1990), higher capacities (Perry and Porter, 1985), new product offerings
(Deneckere and Davidson, 1985), and asymmetry among firms (Compte et al.,
2002). As such, consolidation has the potential for conflicting effects on the
likelihood of collusion. More broadly, whenever counterfactual policies
involve richer changes to more than one variable, predicting the resulting
effect on the selected equilibrium can become substantially more challenging.

In this paper we evaluate a model of equilibrium selection constructed over
the theoretical primitives; a model capable of integrating counterfactual
shifts to many primitives at the same time. In doing this, we build on
experimental studies of the infinitely repeated prisoner’s dilemma (RPD),
where strategic uncertainty has been offered as an explanatory model for
rationalizing several findings across this literature. Specifically, Dal Bó
and Fréchette (2011) outline the organizational power of a selection notion
from Harsanyi and Selten (1988) when applied to data from their experimental
treatments.222A subsequent meta-study across the literature (Dal Bó and
Fréchette, 2018) confirmed the pattern. The central idea here is to formally
model the strategic uncertainty surrounding the collusive, history-dependent,
equilibrium. In so doing, the analyst can reduce the equilibrium-selection
problem to an understanding of the risk/reward trade-off over collusion
attempts. The developed strategic-uncertainty measure is therefore a pure
function of the primitives of the game. Thus, the model can help understand
the trade-offs between two or more competing shifts of the primitives—for
example, a change to the payoffs that increases the rewards to successful
collusion combined with a reduction to the discount rate that makes such an
attempt riskier. The model mediates the effects of any multivariate change
into a single dimension, the effect on strategic uncertainty, which can then
be used to predict the eventual likelihood of collusion. However, while the
literature has shown the explanatory power of the strategic-uncertainty
measure, previous studies have not been designed to test it, to examine the
mechanism, and its potential limitations.

To stress test this equilibrium-selection model we expand the set of
primitives under consideration. In so doing we introduce a new source of
strategic uncertainty to the repeated environment, one that plays an important
role in applications, as motivated by our industry consolidation example
above. Similar to the original two-player RPD experiments, our treatments will
manipulate payoff primitives (primarily a stage-game payoff-parameter $x$)
that affects the riskiness of collusion. But we also manipulate the number of
players within the environment ($N$), where collusion in the model becomes
riskier in larger groups. Hence, we can study joint changes in both $x$ and
$N$—changes that push the equilibrium selection in two different directions,
where the model’s ability to predict the joint effect is the object of
interest. As such, we will test the main hypothesis that equilibrium-selection
across two distinct sources can be understood through the strategic-
uncertainty model. We therefore construct treatment manipulations that modify
$x$ and $N$ relative to a baseline in a way that the strategic-uncertainty
measure is held exactly constant. Finding constant cooperation across the
double-barreled change would be consistent with the modifications to $x$ and
$N$ being perfect substitutes, per their modeled effect on strategic
uncertainty.333Our treatments also include manipulations where the strategic-
uncertainty effects of one of the two variable changes theoretically dominates
the competing effect, with a predicted effect on selection. Moreover, the
design also embeds comparative-static comparisons where a single variable is
manipulated. Complementing the construction and test of the core strategic-
uncertainty model, our design also embeds an alternative hypothesis (which we
characterize the behavioral underpinnings of) in which the group-size variable
$N$ does not affect strategic uncertainty, with a clearly distinct set of
predictions from our main model.

Our main results allow us to clearly separate and validate the equilibrium-
selection model based on strategic uncertainty. Across the six possible
treatment comparative-statics in our design, four are predicted to have clear
directional effects on selection (with the other two being perfect
substitutes). In every single one of these four comparisons, data from our
experiments move in the predicted direction, with effects sizes that are both
statistically and economically significant. This is true for both initial and
ongoing behavior for the repeated games we examine. The more-challenging
comparisons involve treatments with compound shifts that move selection in
opposed directions. Two of our treatment comparisons are constructed so that
changes across the payoff and group-size are perfectly substituting as
captured by the strategic-uncertainty model. Relative to successful
coordination on the collusive outcome, the metric that likely matters most for
applications, our results show strong support for the selection model, and our
designed shifts to the payoffs and number of players are direct substitutes.
Meanwhile, we document discrepancies between the measure’s predictions and
behavior in the first period of interaction. As such, our results indicate
that the extended selection model is more accurate in predicting ongoing
collusion than in predicting initial intentions—where changes in $N$ provide
the key variation to identify this. Overall, our results validate the
theoretical model, providing a tool to understand which effects might dominate
in counterfactuals where policy shifts over multiple primitives. In
particular, the results lend credence to the idea that a reduction of the
environment to a single dimension capturing strategic uncertainty can be
predictive of equilibrium selection.

Uncertainty regarding the other players’ actions is put front-and-center in
our main treatments as the driver of equilibrium selection. Hence, if
strategic uncertainty is the causal mechanism driving selection, then removing
or reducing the doubts about others’ play should make the selection model’s
predictions moot. We pursue this idea in an additional set of treatments where
we allow for pre-play communication in a setting where we would otherwise
expect little collusion. Participants are given the opportunity to exchange
free-form messages prior to the repeated game, a feature that can be used to
reduce uncertainty over others’ intentions (see Kartal and Müller, 2018). For
the same experimental parameterization where we observe ongoing cooperation
rates below one percent without communication, the effect from adding it is to
shift behavior to the other extreme: with initial (ongoing) cooperation rates
of 95 (80) percent.444As a check that the provided communication channel is
not driving results separate from the equilibrium coordination effects, we
implement a second treatment with communication but where the collusive
outcome is not a robust equilibrium outcome. Here we find that communication
does not lead to successful collusion. In other words, communication only has
an effect when there are clear theoretical incentives for collusion. Given
these results, we conclude that strategic uncertainty, the mechanism
underlying the model, is the causal channel. In addition to mechanism
validation, these results clearly outline the limitation of the model to
understanding _tacit_ collusion, in the sense that it fails to provide useful
guidance when collusion is more explicit.

In terms of the paper’s organization, we next outline the related literature.
In section 2 we outline our generalization of the selection model from the
two-player repeated PD game, outline the predictions from that literature, and
provide design details. In section 4 we analyze the results from our core
treatments and demonstrate the model’s predictive properties generalize to
$N$. Section 5 then examines some extensions: one showing that our results
hold for both between- and within-subject identification; and the other
pinning down the strategic uncertainty mechanism via the opportunity for
explicit collusion. Finally, in section 6 we conclude.

###  1.1. Literature

Our paper builds on the recent consolidation of the experimental RPD
literature presented in Dal Bó and Fréchette (2018). While one of our baseline
treatments replicates a standard finding in the literature,555As pointed out
in Berry, Coffman, Hanley, Gihleb, and Wilson (2017) many experimental
replications become harder to find where the papers do not explicitly point
out the replication components. our core contribution is to generalize the
equilibrium selection model outlined in the meta-study, adding an additional
source of strategic uncertainty: the number of players, $N$.666The extension
of the notion of equilibrium selection described in Harsanyi and Selten (1988)
to the RPD was first proposed by Blonski and Spagnolo (2015) and first shown
to organize data by Dal Bó and Fréchette (2011). See also Fudenberg et al.
(2010) for an examination of the effects with imperfect monitoring, and Kartal
and Müller (2018) for a test of a selection theory based on individual
heterogeneity in preferences over dynamic strategies. Where the literature has
developed this model to be explanatory, our approach is both to expand the
selection model to a new setting, but also to take the model as the core
experimental object to be tested.

Our generalization of the strategic uncertainty model in the RPD literature is
carried out in two alternative ways. The first extension (and most-standard,
given its use of independent beliefs) formalizes a distinct source of
strategic uncertainty from the payoff-based source in the meta-study. An
alternative extension (based on fully correlated beliefs) reflects a null
effect, that the newly introduced source has no effect. As such, our
generalization offers a potentially profitable design approach for future
research examining other channels for strategic uncertainty
effects—asymmetries in the action space or payoffs, the effects of
sequentiality, etc.777See Ghidoni and Suetens (forthcoming) and Kartal and
Müller (2018) for experimental examinations the effect sequentiality has in
RPD settings through a reduction in strategic uncertainty.

Our environment also allows us to better distinguish between the empirical
measures linked to the selection model. That is, using literature-level data
assembled by Dal Bó and Fréchette (2018), we show that the two-player RPD
strategic uncertainty model predicts both initial and ongoing cooperation
well. However, neither is identified particularly well from the other. With
more than two players though, this is no longer the case, where we use this to
demonstrate that the developed strategic uncertainty model is better suited
for predicting successful collusion rather than initial intentions.888Ongoing
cooperation is a measure that is likely to be more relevant for empirical
applications where collusion may be a worry. For instance, from Harrington et
al. (2016), page 256: “(…) collusion is more than high prices, it is a mutual
understanding among firms to coordinate their behavior. (…) Firms may
periodically raise price in order to attempt to coordinate a move to a
collusive equilibrium, but never succeed in doing so; high average prices are
then the product of failed attempts to collude.

This paper is part of a broader literature seeking to understand and document
regularities in equilibrium selection. In particular, regularities that are
amenable to theoretical modeling. To this end, the strategic-uncertainty
measure that we examine is particularly promising, as the equilibrium objects
required for calculation are computationally simple: the stationary non-
collusive equilibrium and the history-dependent collusive equilibrium. In
environments beyond the RPD where the equilibrium outcomes are held constant,
the model can be similarly extended per our illustration with a move to $N$
players. However, in more complex environments where the equilibrium set
changes more substantively, the constraint to two focal equilibria in the
strategic uncertainty model may lose validity, and/or raise questions as to
which two strategies are focal. Examples of more-complex settings includes
dynamic games, where the stage environment can change across the supergame and
the space of strategies becomes substantially larger. Vespa and Wilson (2020)
focus on a horse-race examination of which two equilibria are focal (from a
wider set of possible alternatives) for rationalizing behavior in dynamic
games. The paper identifies a similar strategic uncertainty measure
constructed around the most-efficient Markov perfect equilibrium and the best
_symmetric_ collusive equilibrium. A strategic-uncertainty model based on
these strategies predicts behavior, where these strategies dovetail with the
repeated-game strategies in the simpler environment studied here.999Work on
equilibrium selection in dynamic games builds on recent contributions in this
area. For example: Battaglini et al. (2012, 2016); Agranov et al. (2016);
Kloosterman (2019); Vespa and Wilson (2019); Rosokha and Wei (2020); Salz and
Vespa (2020); Vespa (2020).

An experimental literature on behavior in oligopolies documents that collusion
clearly responds to the number of players. Both Cournot (Huck et al., 2004;
Horstmann et al., 2018) and Bertrand settings (Dufwenberg and Gneezy, 2000)
indicate that as the number of players increases collusion becomes less
likely, often as soon as $N$ exceeds two.101010See also references in Potters
and Suetens (2013) for similar findings. We contribute to this literature on
two margins. First, papers here focus on out-of-equilibrium behavior in
settings with a finite-time horizon, and a subsequently unique theoretical
prediction. In contrast, we examine how changes to $N$ affect outcomes in an
infinite-horizon environment with both collusive and non-collusive equilibria.
Second, and crucially, our focus is not just on the qualitative directional
effects from $N$, but on validating a model of how it affects strategic
uncertainty. The model allows for an understanding of the extent of
substitutability between primitives under consideration; and where validated
can predict the directional effects of more-nuanced, multi-dimensional
counterfactuals. Clearly, any equilibrium-selection notion suggested for such
a task requires a great-deal of scrutiny. However, our findings do suggest
substantial optimism that this path may be fruitful.

Our work is also related to an experimental literature on mergers that
manipulates the number of players. As surveyed by Goette and Schmutzler
(2009), some experiments deal with a “pseudo-mergers,” where a subset of the
original firms remain in the market (Huck et al., 2007, for example). Others
experiments implement “real mergers,” where mergers introduce other changes in
the market beyond $N$ (Davis, 2002). A contribution of our approach is that
the strategic-uncertainty measure can predict counterfactual behavior in both
settings. Another discussion in this literature is whether merger effects are
evaluated within the same group of participants (within-subject designs) or
across different groups (between-subject design). In this paper, while our
main treatments make use of between-subject identification, we also conduct
within-subject sessions at the same parameterization, demonstrating that
though there can be meaningful short-run differences, with enough experience
the results do not depend on the approach.111111Differences in behavior can be
stickier if changes are small or introduced gradually. Weber (2006) shows that
increasing the number of players gradually in a coordination game leads to
different results relative to a situation when play starts with a large group.
In repeated games gradual introduction of changes to the payoff primitives
have also been found to have effects in repeated games, see Kartal et al.
(2017). These results suggest that the selection-notions we are examining are
relevant for ‘large’ counterfactual changes, and where future research can
help clarify how to integrate ‘large’ into a predictive model of selection.

The effects of communication devices as a bolster for collusion are well-
established in the experimental literature. As surveyed in Cason (2008) and
Harrington, Gonzalez, and Kujal (2013), more-structured, limited forms of
communication usually result in small, temporary collusive gains, where free-
form communication generates large, long-lasting effects.121212For further
details on the effect of communication in repeated games with an unknown time
horizon, see Fonseca and Normann (2012), Cooper and Kühn (2014), Harrington et
al. (2016), Wilson and Vespa (2020) and Fréchette et al. (2020). For these
reasons, in one of our extensions we examine unrestricted chat messages as a
strong coordination device. The collusive results here clearly indicate that
the domain for our strategic-uncertainty measure based on tacit-collusion does
not include environments where explicit collusion is likely. However, we do
show that there are clear limits on the effects of explicit collusion, and
that these limits are directly predicted by theory. Using a change to the
payoff primitives (here the discount rate) we make collusion a knife-edge,
non-robust equilibrium, and show that the effects of communication are
entirely dissipated.

While much of the literature on repeated games studies the standard two-player
PD game, there is a large literature studying a canonical $N$-player social
dilemma: the voluntary contribution public-goods game (see Vesterlund, 2016,
for a survey). Though much of this literature focuses on finite
implementations, one notable exception is Lugovskyy et al. (2017). Similar to
our paper, the authors use experimental variation over both $N$ and the payoff
primitives (in their case the return to group contribution). However, this is
done with a different end goal. They design offsetting variation in the
payoffs and $N$ to identify the isolated effect of the stage-game’s MPCR. We
instead do so to isolate strategic uncertainty, to test a predictive theory of
selection.

Beyond social dilemmas, our paper is also connected to the literature on
coordination games (see Devetag and Ortmann, 2007, for a survey). The
strategic-uncertainty measure examined in our paper works because the
infinitely repeated prisoner’s dilemma game has a stag-hunt normal-form
representation (Blonski and Spagnolo, 2015), adapting the risk-dominance
notion for one-shot coordination games in Harsanyi and Selten (1988).131313The
difference in our setting is that neither total payoffs nor strategic choices
are directly provided to participants, as these are extensive-form objects.
Instead they are provided with the stage-game payoffs/actions, where
strategies (such as the grim trigger or tit-for-tat) and gross payoffs must be
endogenously formulated. Risk dominance (and the cardinal implementation
through the measure of strategic uncertainty) has been shown to have
substantial predictive content in simple coordination games with trade-offs
over payoff-dominance and risk-dominance (see Battalio et al., 2001; Brandts
and Cooper, 2006, and references therein). Strategic uncertainty has therefore
demonstrated its usefulness as a theoretical selection device both in directly
presented one-shot games, and in repeated games. Our contribution to this
literature is to design an experiment to explicitly test it and show that the
predictive effects extend further still, to multi-player infinite-horizon
settings.

##  2\. Generalizing the Basin of Attraction

Developing empirical criteria for equilibrium selection in games where
collusion is possible requires two measures: one theoretical, one empirical.
On the theory side we need a prediction, a model that maps the primitives of
the game into a scalar where upward/downward movements are clearly
interpretable as increasing/decreasing the likelihood of collusion. On the
empirical side we need a precise target against which the theoretical notion
can be contrasted and validated. This empirical measure should examine a
behavior that differs starkly under the collusive and non-collusive
equilibria.

We begin this section by summarizing the progress made towards validating a
theoretical prediction in the two-player infinitely repeated prisoner’s
dilemma (RPD) literature. The theoretical notion here is the size of the basin
of attraction for the strategy _always defect_. The focal outcome measure is
the cooperation rate of individual players in the initial rounds. In what
follows we discuss the issues as we extend the exercise to a new source of
strategic uncertainty, the number of players $N$—both for the theoretical and
empirical measures.

###  2.1. Two-players

Consider an RPD with discount rate $\delta\in(0,1)$. In each period
$t=1,2,\ldots$ players $i\in\left\\{1,2\right\\}$ simultaneously select
actions $a_{i}\in\mathcal{A}:=${(C)ooperate, (D)efect}. The period-payoff for
player $i$ is a function of both players’ choices, $\pi_{i}(a_{i},a_{j})$,
where all symmetric PD games can be expressed in a compact form by normalizing
all payoffs relative to the joint-defection payoff $\pi_{0}=\pi(D,D)$, and
rescaling with the relative gain from joint cooperation:
$\Delta\pi:=\pi_{i}(C,C)-\pi_{0}$.141414More exactly, game payoffs $\pi$ can
be transformed via $\tilde{\pi}=(\pi_{i}-\pi_{0})/\Delta\pi$ to measure all
payoffs relative to joint defection in units of the optimization premium.
Defining scale and normalization in this way, the PD stage-game can be
expressed with two parameters $g$ and $s$ for the different-action payoffs
$\pi_{i}(D,C)=\pi_{0}+(1+g)\Delta\pi$ and
$\pi_{i}(C,D)=\pi_{0}-s\cdot\Delta\pi$. The parameters $g>0$ and $s>0$ thereby
capture the relative temptation- and sucker-payoff parameters, respectively.

The RPD payoffs can be used as primitive inputs into a risk/reward model of
collusion based upon strategic uncertainty. Strategic uncertainty here is
distilled into a decision between two focal extensive-form RPD strategies:

  1. (i)

Always defect, $\alpha_{\text{\tiny All-D}}$, which plays the stage-game Nash
in all rounds (the unique MPE of the game).151515A Markov strategy is history
independent, removing any conditioning on past play. A Markov-perfect
equilibrium (MPE) is a subgame-perfect equilibrium (SPE) in which agents use
Markov strategies. In an RPD, if choices are forced to be history independent
then there is a unique equilibrium: playing the stage-game Nash equilibrium in
all periods.

  2. (ii)

The Grim Trigger, $\alpha_{\text{\tiny Grim}}$, a strategy that begins by
cooperating but switches to always-defect after observing any defections in
past play (the best-case collusive SPE).161616The strategy here is ‘best case’
in three senses: (i) it can support the best-case outcome; (ii) it uses the
harshest possible punishment, and so can support collusion at smaller values
of $\delta$ than any other strategy; and (iii) any realized miscoordination is
minimal, being resolved in a single round.

As functions of the observable history $h_{t}$, these two strategies are given
by:

$\displaystyle\alpha_{\text{\tiny Grim}}(h_{t})$
$\displaystyle=\begin{cases}C&\text{if }t=1\text{ or
}h_{t}=((C,C),(C,C),\ldots,(C,C)),\\\ D&\text{otherwise;}\end{cases}$
$\displaystyle\alpha_{\text{\tiny All-D}}(h_{t})$ $\displaystyle=D.$

Strategic uncertainty in the two player RPD is measured through the _size of
the basin of attraction for always defect_. The model considers the expected
payoff to player $i$ when uncertainty on the other player $j$ is represented
by a believed strategy mixture $p\cdot\alpha_{\text{\tiny
Grim}}\oplus(1-p)\cdot\alpha_{\text{\tiny All-D}}$. The basin for always
defect is defined as the set of beliefs $p$ for which player $i$ yields a
higher expected payment from $\alpha_{\text{\tiny All-D}}$ than
$\alpha_{\text{\tiny Grim}}$. The always-defect belief basin is therefore the
interval $[0,p^{\star}(g,s,\delta)]$, where the critical-point/interval-width
is given by:171717 In the case that the strategy $(\alpha_{\text{\tiny
Grim}},\alpha_{\text{\tiny Grim}})$ is not an SPE of the repeated game, the
basin size for always defects is defined as $p^{\star}(x_{T},x_{S},\delta)=1$.

(1) $p^{\star}(g,s,\delta)\equiv\dfrac{(1-\delta)\cdot
s}{\delta-(1-\delta)\cdot\left(g-s\right)}.$

The basin-size $p^{\star}(g,s,\delta)$ has a clear interpretation for
strategic uncertainty: for any belief $p>p^{\star}(g,s,\delta)$ on the other
player using the collusive strategy $\alpha_{\text{\tiny Grim}}$, the player
does strictly better choosing $\alpha_{\text{\tiny Grim}}$; for any belief
$p<p^{\star}(g,s,\delta)$, they do strictly better by selecting the non-
collusive strategy $\alpha_{\text{\tiny All-D}}$. As such, the smaller
$p^{\star}$ is, the lower the strategic uncertainty surrounding collusion.
Moreover, the cardinal basin-size measure directly implies the ordinal risk-
dominance relationship between the two strategies. If
$p^{\star}(g,s,\delta)<\nicefrac{{1}}{{2}}$ then the collusive strategy
$\alpha_{\text{\tiny Grim}}$ risk-dominates $\alpha_{\text{\tiny All-D}}$, and
vice versa. Henceforth, by ‘basin of $p^{\star}$’ we mean the maximal belief
on the other cooperating for which the strategy $\alpha_{\text{\tiny All-D}}$
is optimal.

Equation (1) represents an easy-to-derive theoretical relationship between the
payoff primitives of the game (here $g$, $s$ and $\delta$) and a critical
strategic belief on the other player’s likelihood of collusion. The
hypothesized relationship is monotone, where the higher is $p^{\star}$, the
lower is the likelihood of cooperation, thereby allowing for unambiguous
directional predictions for any counterfactual change in the primitives. The
posited mechanism within this model is also clear-cut: strategic uncertainty
introduces a risk/reward trade-off for collusion attempts, which can be solved
using standard economic analysis. This has two benefits: First, we can test
the underlying strategic-uncertainty mechanism through other channels outside
of the model, where we will do exactly that in an extension examining
coordination devices. Second, the necessary assumptions for extending this
model to analyze alternative strategic-uncertainty sources are
straightforward.

(a) Initial cooperation (b) Ongoing cooperation

Figure 1. Meta-study relationship: Strategic Uncertainty and RPD Cooperation

Note: Figures show estimated effects and 95-percent confidence intervals for
initial/ongoing cooperation in RPD meta-study (Dal Bó and Fréchette, 2018).
Red dashed line in Panel (B) indicates implied theoretical relationship for
ongoing cooperation based on the estimated relationship illustrated in Panel
(A). Each point indicates a separate treatment, with the number of
participants indicated.

We now turn to the empirical criteria used to validate this theoretical
measure. As a summary of the RPD literature we focus on the recent meta-study
on the two player RPD (Dal Bó and Fréchette, 2018). Two of the main results
here are to show that the scalar basin-size measure of strategic uncertainty
is highly predictive of behavior, though with a non-linear relationship. We
illustrate this relationship in Figure 1 for two empirical outcome measures.

In both panels in Figure 1 the theoretical measure of strategic uncertainty
(the basin-size $p^{\star}$) is presented on the horizontal axis. The
empirical outcome measures are presented on the vertical axes. In Panel (A) we
present the results for _initial cooperation_ in the supergame, a measure
tracking collusive _intentions_ at the individual level as there is no
interaction with matched partners at this point. In contrast, in Panel (B) we
present results for _ongoing cooperation_ , choices in rounds two and beyond,
a measure of the extent to which collusion attempts are successful. While
there is no mechanical relationship between initial and ongoing cooperation,
the theoretical model used in the basin construction posits an indirect
linkage between the two. If collusion functions through conditional-
cooperation with grim-trigger punishments, then the expected ongoing
cooperation rate is the probability that the players jointly cooperate in the
first round: the initial cooperation rate all squared. Thus, the posited
relationship between initial and ongoing cooperation in the two-player RPD is
not separately identifiable through any of the underlying payoff primitives.

Using the meta-study data from 996 participants across 18 experimental
treatments, we estimate the relationship between late-session cooperation
(supergames 16–20, the data we focus on in our experiments) and the strategic-
uncertainty basin-size measure. Per the meta-study, the fitted relationship is
estimated using a piecewise–linear probit model.181818Individual-level
cooperation decisions are the left-hand side variable, where the basin-size
enters the right-hand side in a piecewise-linear fashion around the risk-
dominance dividing point. The econometric specification is motivated by Dal Bó
and Fréchette (2018, Table 4); however to enforce level-continuity in the
estimated relationship we remove a degree of freedom from their specification
that allowed for a discontinuity at $p^{\star}=\nicefrac{{1}}{{2}}$. The solid
line in each figure indicates the predicted cooperation rate at each
$p^{\star}$ from the probit estimates, where the shaded region indicates the
95 percent confidence interval for the prediction (clustering by treatment).
For both initial and ongoing cooperation the same pattern is found: a
consistently low cooperation level when always-defect is risk dominant
($p^{\star}>\tfrac{1}{2}$); and a significantly decreasing relationship with
$p^{\star}$ when collusion is risk dominant ($p^{\star}<\tfrac{1}{2}$). As
such, Figure 1(A) illustrates Results 3 and 4 from the meta-study.

Figure 1(B) indicates a similar qualitative relationship between strategic
uncertainty and ongoing cooperation. Going beyond just the form though,
layered on top of the estimated ongoing-cooperation relationship we also
indicate the implied theoretical relationship with the initial-cooperation
results. Using the square of the estimated _initial_ cooperation rate given in
Panel (A) we therefore calculate the predicted _joint_ cooperation rate in
round one. Under grim-trigger coordination, the initial joint-cooperation rate
is exactly the ongoing cooperation rate, and so we illustrate this implied
relationship in Panel (B) as the red dashed line. There are certainly some
differences between the estimated relationship using actual ongoing
cooperation decisions (black solid line) and the implied rate from initial
cooperation (red dashed line). However, as the figure illustrates, these
differences are mostly in levels for the region where always-defect is risk
dominant.191919In particular, we find significantly more ongoing cooperation
when the basin measure is above $\nicefrac{{1}}{{2}}$ than we might expect
from the initial rates and the use of a grim-trigger. This is consistent with
another finding in the literature, the frequent use of more-forgiving/lenient
strategies than grim. Tit-for-tat, for instance, can generate substantial
_ongoing_ cooperation when matched with its variant that starts out defecting.
Slopes and levels for $p^{\star}$ in the $[0,\tfrac{1}{2}]$ region where the
strategic uncertainty input has a clearer empirical response are not
significantly different. The implication from this is that with only two
players we cannot separately identify the extent to which the strategic-
uncertainty measure is predicting initial intentions and/or successful
coordination. However, as we will show, adding more players provides a channel
to identify between the initial and ongoing measures.202020For any setting
where collusion requires $N$ agents to initially cooperate to produce ongoing
cooperation then the relationship is simply initial cooperation rate to the
$N$-th power. Separate identification between the two measures then comes
about through comparison across treatments with different values of $N$.

###  2.2. Extending to $N>2$

We now extend the strategic-uncertainty model above to an $N$-player
environment. The core extension is intuitive: instead of considering one other
player choosing a mixture $p\cdot\alpha_{\text{\tiny
Grim}}\oplus(1-p)\cdot\alpha_{\text{\tiny All-D}}$, we consider $N-1$ other
players choosing this same strategic mixture.

To outline the extension, and set-up our design, we consider a family of
symmetric social dilemmas that nest the standard RPD when $N=2$. However, to
hold constant a $2\times 2$ stage-game representation for all $N$, our family
of dilemmas make use of an aggregate (and deterministic) signal of the other
agents’ actions. Each player $i=1,\ldots,N$ continues to make a binary action
choice $a_{i}\in\mathcal{A}\equiv\left\\{C,D\right\\}$, but their payoffs do
not vary with (and they do not receive feedback on) the separate actions of
the other $N-1$ players. Instead, payoffs are determined by the own-action
$a_{i}$ and a deterministic binary signal
$\sigma(a_{-i})\in\left\\{S\text{(uccess)},F\text{(ailure)}\right\\}$ of the
others’ actions, $a_{-i}$. In particular, the generic player $i$’s stage-game
payoff and signal function are given, respectively, by:

$\displaystyle\pi_{i}\Bigl{(}a_{i},\sigma\Bigr{)}$
$\displaystyle=\begin{cases}\pi_{0}+\Delta\pi&\text{if }a_{i}=C,\sigma=S,\\\
\pi_{0}+\Delta\pi\cdot\left(1+x\right)&\text{if }a_{i}=D,\sigma=S,\\\
\pi_{0}-\Delta\pi\cdot x&\text{if }a_{i}=C,\sigma=F,\\\ \pi_{0}&\text{if
}a_{i}=D,\sigma=F;\end{cases}$ $\displaystyle\sigma(a_{-i})$
$\displaystyle=\begin{cases}S&\text{if }a_{j}=C\text{ for all }j\neq i,\\\
F&\text{otherwise.}\end{cases}$

These choices lead to a symmetric game, where payoffs can be summarized with a
$2\times 2$ table over: (i) the own action $C$ or $D$; and (ii) the signal
outcome, an $S$ signal if the other $N-1$ players jointly cooperate, or an $F$
signal if at least one matched player defects. The exact payoffs (with the
same implicit scale $\Delta\pi$ and normalization $\pi_{0}$ as before)
implement a PD-like environment where payoff-based strategic uncertainty is
collapsed to a single parameter $x$.212121In the meta-study notation this is
implemented with $s=g=x$. This single-parameter formulation is equivalent to
the Fudenberg et al. (2010) benefit/cost formulation, where their benefit/cost
ratio $b/c$ parameter is given by $\nicefrac{{(1+x)}}{{x}}$ here.

The success/failure signal here is a deterministic function of the $N-1$ other
player’s actions that dovetails with the standard RPD game when $N=2$. The
choice for the signal function $\sigma(\cdot)$ here maximizes the coordinative
pressure, duplicating a Bertrand-like tension: collusion is successful only
when the other $N-1$ players all cooperate.222222While potentially
interesting, one disadvantage of a Cournot-like parameterization where the
positive externality from others’ cooperation is strictly increasing in the
number of cooperators is that the cardinality of the signal/history spaces
will then scale with $N$. However, note that the precise basin-size formula is
_identical_ under the Cournot formulation if own cooperation has an additive
cost $x\cdot\Delta\pi$ and the punishment path is triggered on _any_ level of
defection. An alternative choice for a signal $\sigma(\cdot)$ that does not
scale with $N$ would be that successes are achieved whenever some minimal
number of players cooperate ($\geq 2$ say). Notice though, that such a choice
introduces a second coordination problem over who cooperates and who defects.
Efficiency requires the minimal number of cooperators, with the rest free
riding. Changing the signal function in this way would therefore introduce a
distributional asymmetry (see Wilson and Vespa, 2020, for an illustration that
these additional dimensions lead to non-trivial problems). Given our focus on
understanding the effects from adding a new source of strategic uncertainty,
we therefore chose an environment that did not introduce additional trade-
offs/confounds.

Ignoring the game’s scale and normalization (held constant in our experiments
with $\Delta\pi=\$9$ and $\pi_{0}=\$11$) the repeated games we examine are
summarized by three primitives: (i) The relative cost of cooperating, $x$.
(ii) The number of players, $N$. (iii) The continuation probability, $\delta$.
Our experiments will fix $\delta=\nicefrac{{3}}{{4}}$ in all but one
diagnostic treatment in the extensions section. This leaves us with two key
experimental parameters: the relative cost $x$ (actual cost $X=x\Delta\pi)$
and the number of participants $N$.

In building a model of strategic uncertainty for arbitrary $N$, we will use a
symmetric belief over the others’ choices. That is, we assume each player
chooses a mixture $p\cdot\alpha_{\text{\tiny
Grim}}\oplus(1-p)\cdot\alpha_{\text{\tiny All-D}}$ over the two
strategies.232323For the $N$-player dilemma we define the grim-trigger
strategy with imperfect-signals as:  $\alpha_{\text{\tiny
Grim}}(h_{t})=\begin{cases}C&\text{if }t=1\text{ or
}h_{t}=((C,S),(C,S),\ldots,(C,S))\\\ D&\text{otherwise.}\end{cases}$ Our
family of social dilemmas require cooperation from all $N$ players for
everyone to get a success signal. Because of this, the strategic uncertainty
reduces to the probability that the other $N-1$ players _jointly_ coordinate
on the collusive strategy,

$Q\left(N\right)=\mbox{Pr}\left\\{N-1\text{ others all choose
}\alpha_{\text{\tiny Grim}}\right\\}.$

In every other case a failure will be received by at least $N-1$ players, and
the punishment path will be triggered.

In an identical manner to the two-player case, the critical belief
$Q^{\star}(N)$ is given by the point of indifference between the amount given
up with certainty from a single round of cooperation, $x\cdot\Delta\pi$, and
the continuation gain from collusion,
$\tfrac{\delta}{1-\delta}\cdot\Delta\pi$, obtained with probability $Q(N)$.
Indifference is therefore given by:

$\displaystyle Q^{\star}\left(N\right)=\frac{(1-\delta)}{\delta}x,$

where the RHS is identical to the two-player construction in (1) for $x=g=s$.

To complete the extension we therefore need to relate the joint-cooperation of
the other $N-1$ players to the probability $p$ that each other player
individually attempts to collude. However, even though we have specified the
marginal belief distribution and assumed symmetry, we must still resolve the
relationship between the joint and marginal distributions: the extent to which
beliefs are correlated. In particular our design and extension will focus on
two extreme models as we extend the model to $N$-players. The ‘standard’
extension, where beliefs are fully independent; and an alternative/null-effect
model where beliefs are perfectly correlated.242424See Cason et al. (2020) for
a clear example of correlated beliefs arising where independence would be the
standard prediction. Assuming perfect correlation for the other $N-1$ agents,
joint and individual probabilities are identical, $Q\left(N\right)=p$, and so
the extended critical belief (and correlated model outcome) is given by:

(2) $p^{\star}_{\text{Corr.}}(x)=\dfrac{1-\delta}{\delta}\cdot x.$

In constrast, when the beliefs are independent we have
$Q\left(N\right)={p}^{N-1}$, and the critical belief (and independent model
extension) is:

(3) $p^{\star}_{\text{Ind.}}(x,N)=\left(\dfrac{1-\delta}{\delta}\cdot
x\right)^{\tfrac{1}{N-1}}\equiv\left(p^{\star}_{\text{Corr.}}(x)\right)^{\tfrac{1}{N-1}}.$

Obviously, when $N=2$ the basin measures in (2) and (3) are identical,
dovetailing with the standard construction. However, for $N>2$ the two
measures of strategic uncertainty are distinct, where the standard model
extension under independence has strategic uncertainty vary both through the
payoff parameter $x$ and the group-size $N$.

##  3\. Experimental Design

The basin of attraction for always defect under independent beliefs serves as
our measure of strategic uncertainty. Ceteris paribus, the greater the
uncertainty on successful strategic coordination, the more likely the subject
is to take refuge in the safer strategy—in the case of an RPD game, the stage-
game Nash outcome of defecting.

As outlined above, as we extend the environments to $N>2$, this opens up a
question as to how strategic uncertainty is affected by $N$. If others’
behavior is thought to be highly correlated, adding players but holding
constant the payoffs will do little to affect the selected behavior in our
games. If this is so, the null-effect $p^{\star}_{\text{Corr.}}$ measure of
strategic-uncertainty will predict behavior. In contrast, in a more-standard
extension where beliefs on the other players are independent, then
$p^{\star}_{\text{Ind.}}$ will model the strategic uncertainty. Under this
extension, we will be able to use shifts in $p^{\star}_{\text{Ind.}}$ to
understand changes in the selected behavior. While one implication of this is
that the addition of more players will ceteris paribus reduce collusion, a
deeper implication of the model is to help us understand substitution effects
across the two sources of strategic uncertainty, $x$ and $N$.

Our experimental design attempts to untangle the effects of strategic
uncertainty. The aim of the design is to embed comparative-static tests on the
effect of $N$ (and so rule out the $p^{\star}_{\text{Corr.}}$ null-effect
model), but also to examine the possible substitution effects by constructing
perfect-substitutes treatments with the $p^{\star}_{\text{Ind.}}$ model. We
achieve this through a series of experimental implementations of the
$N$-player 2-action–2-signal repeated game outlined above. In particular, the
first part of our design will use this family of games to distinguish and
separate between the two extremes of independence and perfect correlation,
leveraging the theoretical relationships derived above.

While we cannot directly manipulate strategic uncertainty—as the basin-size
measures are indirect, theoretical relationships derived from the
primitives—equations (2) and (3) allow us to implicitly manipulate each
measure through shifts in $x$ and/or $N$. Increases in $x$ increase the
strategic uncertainty in both models: as higher costs of cooperation require a
greater belief that the other(s) are cooperating. In contrast, increases to
the number of players $N$ only increases strategic uncertainty for the
independent basin-size measure, interacting with $x$ in a non-linear manner.

Using equations (2) and (3), the two notions can be varied in isolation from
one another. As such, it is possible to construct a $2\times 2$ design that
orthogonally varies each strategic-uncertainty measure. Next, we outline our
design, summarized in Table 1.

Panel (A) of Table 1 illustrates our first treatment dimension, which
manipulates the payoff cost of cooperating $X=x\cdot\Delta\pi$, where
$\Delta\pi=\$9$. The two values of $X$—a high temptation of $\$9$ (illustrated
on the left, $x=1$), and a low temptation of $\$1$ (on the right,
$x=\nicefrac{{1}}{{9}}$)—lead to two payoff environments over own-actions and
the signals. The given stage-game payoffs capture what a participant would see
on their screens.252525See Figure A.3 in the Online Appendix for
representative screenshots.

Table 1. Experimental Design

Panel A.  Stage-game payoffs | $X=\$9$ |  | $X=\$1$
---|---|---|---
$\sigma(a_{-i})=S$ | $\sigma(a_{-i})=F$ |  | $\sigma(a_{-i})=S$ | $\sigma(a_{-i})=F$
Coop., $\pi_{i}(C,\sigma)$ | $\$20$ | $\$2$ |  | $\$20$ | $\$10$
Defect, $\pi_{i}(D,\sigma)$ | $\$29$ | $\$11$ |  | $\$21$ | $\$11$
Panel B.  All-D Basin Size |  $X=\$9$ ($x=1$) |  |  $X=\$1$ ($x=\nicefrac{{1}}{{9}}$)
$N=2$ | $N=4$ |  | $N=4$ | $N=10$
Cor. basin, $p^{\star}_{\text{Cor.}}(x)$ | $p^{\star}_{0}$ | $p^{\star}_{0}$ |  | $p^{\star}_{0}-\Delta p^{\star}_{\text{Cor.}}$ | $p^{\star}_{0}-\Delta p^{\star}_{\text{Cor.}}$
| [0.33] | [0.33] |  | [0.04] | [0.04]
Ind. basin, $p^{\star}_{\text{Ind.}}(x,N)$ | $p^{\star}_{0}$ | $p^{\star}_{0}+\Delta p^{\star}_{\text{Ind.}}$ |  | $p^{\star}_{0}$ | $p^{\star}_{0}+\Delta p^{\star}_{\text{Ind.}}$
| [0.33] | [0.69] |  | [0.33] | [0.69]
Sessions | 3 | 3 |  | 3 | 2
Subjects | 60 | 60 |  | 72 | 60
Panel C.  Meta-study predictions | $p^{\star}_{0}$ | Marginal effect from:
[0.33] | Basin increase to [0.69] | Basin decrease to [0.04]
Initial coop. ($t=1$) | $0.50$ | $-0.26$ | $+0.35$
Ongoing coop. ($t>1$) | $0.37$ | $-0.21$ | $+0.50$

Note: Meta-study prediction indicates the cooperation-rate estimation from the
2-player basin recovered from the treatment-clustered probits illustrated in
Figure 1.

Our design also manipulates the number of players $N$, captured in the column
headings of Panel (B) in Table 1. In total, we create four treatment
environments, each defined by an $(N,X)$-pair, where we will refer to
treatments with the directly varied parameter pair. In Panel (B), the
rightmost four columns are headed by the chosen game variable, where the two
rows of the table indicate how these choices affect the two basin-size
measures of strategic uncertainty.

To manipulate each basin-size measure separately, our design takes
$\left({}^{N=2}_{X=\$9}\right)$ as its starting point. The values for both the
independent and correlated basin-size measures are the same:
$p^{\star}_{0}=0.33$. Holding the relative cooperation cost fixed and
increasing the number of players to $N=4$ does not affect the correlated
measure in (2). However, a shift to $N=4$ increases the independent basin
measure to $p^{\star}_{0}+\Delta p^{\star}_{\text{\footnotesize{Ind.}}}=0.69$.

Now consider the manipulation of $X$. Comparing
$\left({}^{N=4}_{X=\$1}\right)$ to $\left({}^{N=2}_{X=\$9}\right)$, we hold
constant the independent basin-size measure at $p^{\star}_{0}=0.33$. The
shifts in both $X$ and $N$ have perfectly substituting effects in equation
(3). However, the same change in both variables under the correlated-basin
measure has a substantial effect, where the change in $N$ does not provide an
offsetting effect. As such, the correlated-basin measure is lowered to
$p^{\star}_{0}-\Delta p^{\star}_{\text{\footnotesize{Corr.}}}=0.04$. Finally,
in the $\left({}^{N=10}_{X=\$1}\right)$ treatment we complete the $2\times 2$
design over the two basin-size measures. Comparing
$\left({}^{N=4}_{X=\$1}\right)$ to $\left({}^{N=10}_{X=\$1}\right)$ holds
constant the correlated basin, which does not depend on $N$, at
$p^{\star}_{0}-\Delta p^{\star}_{\text{\footnotesize{Corr.}}}=0.04$. But the
increased number of players does increase strategic uncertainty in the
independent basin. In particular, our parameterization matches the independent
basin sizes for $\left({}^{N=10}_{X=\$1}\right)$ and
$\left({}^{N=4}_{X=\$9}\right)$ at $p^{\star}_{0}+\Delta
p^{\star}_{\text{\footnotesize{Ind.}}}=0.69$.

Through variation in the primitives $x$ and $N$, our design thereby generates
four correlated/independent basin measure pairs with a $2\times 2$
structure:262626We note that our choices of $\Delta\pi=\$9$ and
$\delta=\nicefrac{{3}}{{4}}$ were necessary choices here, as we aimed for
exact-integer solutions for $N$ and $X$ for simplicity of the presentation.
Our design over the basin measures is more-exactly given by:
$\left(p^{\star}_{\text{Corr.}},p^{\star}_{\text{Ind.}}\right)\in\Bigl{\\{}3^{-1},3^{-3}\Bigr{\\}}\times\Bigl{\\{}3^{-1},3^{-1/3}\Bigr{\\}}.$

$\left(p^{\star}_{\text{Corr.}},p^{\star}_{\text{Ind.}}\right)\in\Bigl{\\{}p^{\star}_{0},p^{\star}_{0}-\Delta
p^{\star}_{\text{\footnotesize{Corr.}}}\Bigr{\\}}\times\Bigl{\\{}p^{\star}_{0},p^{\star}_{0}+\Delta
p^{\star}_{\text{\footnotesize{Ind.}}}\Bigr{\\}}:=\Bigl{\\{}0.33,0.04\Bigr{\\}}\times\Bigl{\\{}0.33,0.69\Bigr{\\}}.$

The design therefore achieves the goal of orthogonal variation over the two
basin measures. However, the parameterization was also chosen so that the
shifts in each dimension would be expected to have quantitatively large
effects. Through the Dal Bó and Fréchette (2018) meta-study we can generate
level predictions for the behavioral effects of each change. Our design
generates three basin-size measures: $p^{\star}_{0}=0.33$,
$p^{\star}_{0}-\Delta p^{\star}_{\text{\footnotesize{Corr.}}}=0.04$, and
$p^{\star}_{0}+\Delta p^{\star}_{\text{\footnotesize{Ind.}}}=0.69$. Using the
probit models illustrated in Figure 1 we leverage the meta-study to make
_quantitative_ predictions for the cooperation rates under each basin-size
measure. These predictions are indicated in Panel (C) of Table 1.

Shifts in the basin-of-attraction under either model generate large changes in
the predicted outcomes. The first column in Panel (C) indicates the baseline
initial (ongoing) cooperation rate expected at $p^{\star}=0.33$ using the
meta-data estimated relationship is 50 percent (37 percent).272727All
predictions based on late-session meta-study data (supergames 16–20), the same
point in the sessions used to assess our hypotheses. The next column pair then
indicates the expected treatment effect for a shift in the strategic
uncertainty level from $p^{\star}=0.33$ to either of the two alternative
values. Panel (C) indicates that if either of the two strategic uncertainty
measures captures and generalize behavior, then we would expect a large
treatment effect on one of the two design dimensions.

We formalize the two competing hypotheses as:

######  Correlated-Basin/Null-effect Hypothesis.

Cooperation increases as we decrease $X$, but there is no effect as we vary
the number of players $N$.

######  Independent-Basin Hypothesis.

Cooperation decreases as we increase $X$ and/or $N$. Moreover, the
substitution effects between $X$ and $N$ indicate no effect on cooperation if
we decrease $X$ and increase $N$ to hold constant the
$p^{\star}_{\text{Ind.}}$ measure of strategic uncertainty.

That is, consider the prediction if the standard independence-based extension
of strategic uncertainty is the correct model. In treatments
$\left({}^{N=2}_{X=\$9}\right)$ and $\left({}^{N=4}_{X=\$1}\right)$ the
independent basin-size is 0.33, increasing to 0.69 in treatments
$\left({}^{N=4}_{X=\$9}\right)$ and $\left({}^{N=10}_{X=\$1}\right)$. If the
strategic uncertainty relationship estimated from the two-player RPD meta-data
is perfectly extrapolated then we should expect: (i) A reduction of 26 (21)
percentage points in initial (ongoing) cooperation across the treatment pair,
caused by the increase in strategic uncertainty. (ii) A null effect on
cooperation within each treatment pair, reflecting the designed perfect
substitution across $X$ and $N$.282828 Alternatively, under a null-effect from
$N$, given by the correlated basin measure, the basin-size is reduced from
0.33 to 0.04 as we move between the $\left({}^{N=2}_{X=\$9}\right)$ and
$\left({}^{N=4}_{X=\$9}\right)$ treatment pair and the
$\left({}^{N=4}_{X=\$1}\right)$ and $\left({}^{N=10}_{X=\$1}\right)$ pair. The
RPD prediction from the meta-study is then for an increase in the initial
(ongoing) cooperation rate of 35 (50) percentage points (and again, a null
effect within each pair).

Notice that our hypotheses are silent with respect to which of the two outcome
measures, initial and/or ongoing cooperation, we are supposed to match. The
two measures have different interpretations—where initial cooperation captures
intentions, and ongoing cooperation captures successful coordination. In the
case of the two-player RPD, Figure 1 shows that the basin size tracks both
cooperation measures relatively well, and that the effects are hard to
disentangle. Through $N$, we are able to generate additional variation in the
theoretical relationship between initial and ongoing cooperation variables
that separates the two relationships on another dimension. An advantage of our
design is that it will allow us to better identify if either of the two
measures is better predicted by either basin-size measure.

### Experimental Specifics

We use a between-subject design over the four distinct environments outlined
in Table 1. Participants for each treatment were recruited from the
undergraduate population at the University of Pittsburgh, participating in
only one session. We recruited a total of 520 participants, with 252 for the
first four treatments and 268 for the extensions that we outline in Section 5.
Three sessions were conducted for each environment, with an aim to recruit at
least 20 participants per session—the one exception to this was the
$\left({}^{N=10}_{X=\$1}\right)$ treatment, where we ran two sessions of
30.292929In more detail, our design called for sessions to have at least 20
participants, but allowed us to recruit an additional group of size $N$
depending on realized show ups. For $\left({}^{N=10}_{X=\$1}\right)$ we
instead opted to recruit 30 for each session so that we had at least three
groups in each supergame. Sessions lasted between 55 and 90 minutes with
participants receiving an average payment of $18.61.

Each session comprised 20 supergames, where supergames used a random
termination chance of $1-\delta=\nicefrac{{1}}{{4}}$ after each completed
round. However, supergame-lengths are matched by session across treatment.
Participants were randomly and anonymously matched together across the 20
supergames in a stranger design.303030All subjects received written and verbal
instructions on the task and payoffs, where instructions are provided for
readers in the Online Appendix. The 20 supergames were divided into two parts
of ten supergames.313131Subjects received full instructions for the first part
and were told they would be given instructions on part two after completing
supergame ten. For the four between-subject treatments outlined in section 3,
part two was then identical to part one. Later in the paper we will outline a
further set of treatments with a within-subject change across the parts. The
design choice for two identical parts here allows for direct comparisons in
first-half play. For final payment, one supergame from each part was randomly
selected, where only the actions/signals from the last round in the selected
supergame counted for payment.323232This method is developed in Sherstyuk et
al. (2013) to induce risk neutrality over supergame lengths. Another benefit
from this design choice is that there are no wealth effects within a
supergame, and where history only matters as an instrument for others’ future
play.

##  4\. Results

In the first section we begin by describing the aggregate treatment-level
cooperation rates. We postpone inferential tests of our two basin-extension
hypotheses to the second section. The main finding here is that while neither
extension contains all the relevant information for predicting initial
cooperation, we do find more definitive results for ongoing cooperation.
Overall, we conclude that the basin-size measure based on a standard
independence assumption contains all relevant information for predicting
successful coordination within the experimental supergames.

Table 2. Cooperation rates and basin-effect decomposition

Panel A.  Action and signal rates | $X=\$9$ |  | $X=\$1$
---|---|---|---
$N=2$ | $N=4$ |  | $N=4$ | $N=10$
Initial coop. | $\underset{\mbox{{\tiny$\left(0.058\right)$}}}{0.503}$ | $\underset{\mbox{{\tiny$\left(0.017\right)$}}}{0.035}$ |  | $\underset{\mbox{{\tiny$\left(0.042\right)$}}}{0.792}$ | $\underset{\mbox{{\tiny$\left(0.055\right)$}}}{0.357}$
Ongoing coop. | $\underset{\mbox{{\tiny$\left(0.055\right)$}}}{0.450}$ | $\underset{\mbox{{\tiny$\left(0.003\right)$}}}{0.006}$ |  | $\underset{\mbox{{\tiny$\left(0.050\right)$}}}{0.409}$ | $\underset{\mbox{{\tiny$\left(0.048\right)$}}}{0.184}$
Initial success | 0.503 | 0.000 |  | 0.578 | 0.000
Ongoing success | 0.450 | 0.000 |  | 0.293 | 0.000
Panel B.  Cooperation decomposition | $p^{\star}_{0}$ | Marginal effect from:
| Ind. basin increase to | Corr. basin decrease to
| [0.33] | $p^{\star}_{0}+\Delta p^{\star}_{\text{\footnotesize{Ind.}}}=[0.69]$ | $p^{\star}_{0}-\Delta p^{\star}_{\text{\footnotesize{Corr.}}}=[0.04]$
Initial coop. | $\underset{\mbox{{\tiny$\left(0.058\right)$}}}{0.464}$ | $\underset{\mbox{{\tiny$\left(0.048\right)$}}}{-0.395}$ | $\underset{\mbox{{\tiny$\left(0.053\right)$}}}{+0.357}$
Ongoing coop. | $\underset{\mbox{{\tiny$\left(0.051\right)$}}}{0.366}$ | $\underset{\mbox{{\tiny$\left(0.051\right)$}}}{-0.293}$ | $\underset{\mbox{{\tiny$\left(0.061\right)$}}}{+0.115}$

Note: Results are calculated using data from the last-five supergames.
Cooperation rates present raw proportions (with subject-clustered standard
errors). The cooperation decomposition runs two subject-clustered probits on
the cooperation decision (initial and ongoing) where variables are dummies for
a low correlated basin treatment ($X=\$1$, both $N$ values) and a high-
independent–basin treatment ($X=\$9/N=4$ and $X=\$1/N=10$). Coefficients shown
are the predicted level at just the constant (the $p^{\star}_{0}$ column) and
the predicted cooperation changes from each estimated dummy.

###  4.1. Main Treatment Differences

The top two lines of Panel (A) in Table 2 report cooperation rates broken out
across the four treatments, where we separately report initial (the first
round) and ongoing cooperation (all subsequent rounds). The averages in the
table are for the last five supergames—late-session behavior, after subjects
have amassed experience in the environment—though including all rounds
generates similar results (see Table A.1 in the Online Appendix). The results
point to large cooperation shifts across both the cost to cooperating $X$ and
the group size $N$.

The initial cooperation rate in our $\left({}^{N=2}_{X=\$9}\right)$ treatment
is 50.3 percent, essentially identical to the 50 percent cooperation rate
predicted by the PD meta-study. However, holding constant the cooperation cost
at $X=\$9$ and doubling the group size to four virtually eliminates
cooperative behavior, with just 3.5 percent initial cooperation in
$\left({}^{N=4}_{X=\$9}\right)$. In low-temptation settings ($X=\$1$), groups
of $N=4$ show highly cooperative behavior (79.2 percent for initial
decisions), while groups of $N=10$ generate moderate cooperation rates (35.7
percent). The second row of Panel (A) indicates the ongoing ($t>1$)
cooperation rate. Here the data indicates a decline in cooperation over the
initial behavior in all treatments, though the quantitative effects are
largest in the $\$X=1$ treatments.333333In the Online Appendix, Table A.2
further breaks out ongoing cooperation by the observed history in the previous
round. The results indicate clear evidence that individual cooperation is
highly conditional on successful coordination. However, strategies are
significantly more-forgiving after failed cooperation at $X=\$1$ than $X=\$9$.

The third and fourth rows of Table 2 present the fraction of participant
rounds where a success signal was observed.343434A success requires that the
other $N-1$ participants jointly cooperate. Success is a direct function of
group-level cooperation, where the _expected_ success rate with an independent
cooperation rate $q$ is $q^{N-1}$. In two-player games, the success rate is
identical to the cooperation rate. For the initial round the expected success
rates (in the Table 2 column order) are: 0.503, $4.2\times 10^{-5}$, 0.497 and
$9.5\times 10^{-5}$. Focusing on success signals, similar patters emerge to
ongoing cooperation, though with starker quantitative effects. While a success
is the modal signal in the $\left({}^{N=2}_{X=\$9}\right)$ and
$\left({}^{N=4}_{X=\$1}\right)$ treatments, in the
$\left({}^{N=4}_{X=\$9}\right)$ and $\left({}^{N=10}_{X=\$1}\right)$
treatments we observe no successes at all.353535As success is a direct
aggregate of individual level cooperation we do not report standard errors
(where we also cannot calculate standard errors when there is no variation).
However, the starkness of the effect with no successes when the independent
basin-size is high make clear the underlying economic effects.

Using just the raw averages in the top panel of Table 2, the evidence clearly
falsifies the correlated-basin/null hypothesis on the effect of $N$, for both
initial and ongoing cooperation. The experimental results indicate large
shifts in behavior as we move $N$ as a comparative-static, fixing the value of
$X$. Fixing $N=4$ we do find the comparative-static effect predicted by the
correlated-basin measure as we move $X$, though this directional effect is
also predicted by the independent basin.

The evidence suggests that the independent-basin hypothesis fares slightly
better. Both initial and ongoing cooperation clearly respond in the predicted
direction as we shift either $X$ or $N$ in isolation. However, for initial
cooperation, we do not find perfect substitution as we move both $x$ and $N$,
as predicted by the independent-basin hypothesis. The hypothesis predicts no
change in cooperation rates comparing either $\left({}^{N=2}_{X=\$9}\right)$
to $\left({}^{N=4}_{X=\$1}\right)$ or $\left({}^{N=4}_{X=\$9}\right)$ to
$\left({}^{N=10}_{X=\$1}\right)$. When this hypothesis is scrutinized using
initial cooperation rates, we find large differences in either
comparison.363636The differences are economically large: 29 percentage points
in the first comparison and 35 percentage points in the second. To see this
finding from a different perspective, let us pool treatments at each value of
$X$. That is, we compare the average initial cooperation rate pooling
$\left({}^{N=2}_{X=\$9}\right)$ and $\left({}^{N=4}_{X=\$9}\right)$ to the
average pooling $\left({}^{N=4}_{X=\$1}\right)$ and
$\left({}^{N=10}_{X=\$1}\right)$. Initial cooperation in the pooled treatments
for $X=\$9$ and $X=\$1$ are 28.6 and 59.4 percent, respectively, and the
difference is more than 30 percentage points. In other words, initial
cooperation rates are inconsistent with the independent-basin hypothesis.

Results for ongoing cooperation though are substantially better for the
independent basin, where $\left({}^{N=2}_{X=\$9}\right)$ and
$\left({}^{N=4}_{X=\$1}\right)$ are not substantially different. We do note a
difference between $\left({}^{N=4}_{X=\$9}\right)$ and
$\left({}^{N=10}_{X=\$1}\right)$, this is primarily driven by the very stark
finding of near-zero cooperation in $\left({}^{N=4}_{X=\$9}\right)$. We
explore this further below. In the aggregate though, pooling the ongoing
cooperation rates across $X$, we find similar rates at 22.8 percent for
$X=\$9$ and 29.8 percent for $X=\$1$.

###  4.2. Evaluation of Independent- and Correlated-Basin Hypotheses

Panel (B) in Table 2 provides a direct statistical evaluation of our two
competing hypotheses. The table reports results of a probit model that
assesses subjects’ cooperation decisions using dummy variables for the
2$\times$2 design in Table 1 Panel (B). The dummy covariates are an indicator
for the $\Delta p^{\star}_{\text{Cor.}}$ decrease in the correlated basin-size
(as we decrease $X$), and an indicator for the $\Delta
p^{\star}_{\text{\footnotesize{Ind.}}}$ increase in the independent basin-size
(as we increase $N$ within each $X$).

Each row in Panel (B) provides the results from a separate estimation, one
over initial cooperation, one over ongoing. The first column reports the
estimated cooperation rate when both dummy variables are zero: essentially the
cooperation rate for a game with a basin size of $p^{\star}_{0}=0.33$. The
final column-pair then report the estimated marginal effect on the cooperation
rate for each basin shock, holding the other constant. If either of the two
basin hypotheses fully explains behavior, we would expect a significant
estimate for the corresponding dummy and an insignificant effect on the other.

The estimation procedure here is designed to directly parallel the probit-
model used to generate predictions from the meta-study. The estimated
cooperation rates at $p^{\star}_{0}=0.33$ is in fact quantitatively very close
to the meta-study prediction in Panel (C) of Table 1. Where the meta-study
predicts an initial (ongoing) cooperation of 49.5 (37.3) percent, our data at
$p^{\star}_{0}=0.33$ indicates similar (and statistically inseparable) rates
of 46.4 (36.6) percent. To illustrate this, in Figure 2 we provide the fitted
relationships from the meta study but where we overlay results from our four
treatments (the smaller circles) using the independent basin-size on the
horizontal axis. In addition we also indicate the results pooled over each
value for the independent basin measure (the larger diamonds). While there is
substantial divergence for initial cooperation in Panel (A), the
quantitatively similar results for ongoing cooperation in Panel (B) are
clear.373737In Figure A.1 in the Online Appendix we present an analogous
figure organized under the correlated basin-size model, illustrating much
poorer organization of the data, both relatively across the treatment
comparisons, and quantitatively.

(a) Initial cooperation (b) Ongoing cooperation

Figure 2. Cooperation and the Independent Basin-Size Model

Note: Figures show pooled data by the independent basin (diamonds) while the
separate treatments are illustrated as the surrounding circles. See Figure A.1
in the appendix for an analogous figure for the correlated basin.

Our tests of the two competing hypotheses are focused on the second and third
columns of Panel (B) in Table 2. If the independent (correlated) basin measure
captures all relevant facets of behavior, we would expect a significantly
negative (insignificant) estimate for the independent-basin increase
(correlated-basin-decrease), and an insignificant (significantly negative)
effect on the correlated (independent) basin-increase.

For initial cooperation, we find that changes to both basin-measures generate
significant effects ($p<0.001$). The magnitudes of each estimated marginal
effect are very similar, though each moving in opposite directions, as
predicted. Since neither effect dominates, we conclude that both $X$ and $N$
contain information for predicting initial cooperation that is not fully
absorbed by either basin measure.

However, consistent with our descriptive presentation of the raw treatment
rates in Table 2 Panel (A), the probit estimates for ongoing cooperation in
Panel (B) do break towards the independent-basin construction. The coefficient
on the increase in the independent basin is negative and significant
($p<0.001$), while the estimate on the decrease for the correlated basin is
much smaller in magnitude and is not significant at the 5 percent level
($p=0.061$). Beyond just the qualitative directional effects, the quantitative
change in ongoing cooperation under the independent-basin measure is close to
the predicted effects from the relevant basin shifts that we would expect from
the RPD meta-study data. That is, the predicted effect from the meta study for
ongoing cooperation when the size of the basin increases from
$p^{\star}_{0}=0.33$ to $0.69$ is a 21 percentage point drop (see Table 1,
Panel C), where our estimates indicate a 29 percentage point drop.383838In
contrast, for a decrease to 0.04 we should expect an ongoing cooperation-rate
increase of 50 percentage points, where we instead we see 11.5 percent.

As alluded to above, the differences on ongoing cooperation rates between our
data and the out-of-sample prediction from the meta-study is driven by the
stark (essentially boundary) behavior in the $\left({}^{N=4}_{X=\$9}\right)$
treatment. As illustrated in Figure 1(B) a two-player repeated game with a a
basin of size $p^{\star}=0.69$ has a predicted ongoing cooperation rate of
16.3 percent, where we should be able to reject 11 percent cooperation at 95
percent confidence. While the $\left({}^{N=10}_{X=\$1}\right)$ treatment is
close to the predicted rate (as are the two other treatments at
$p^{\star}=0.33$), Figure 1(B) clearly indicates the
$\left({}^{N=4}_{X=\$9}\right)$ treatment being significantly below the
prediction. However, when the non-collusive strategy is risk dominant (when
the independent basin size is greater than $\tfrac{1}{2}$), the argument made
in the literature is that we should not expect substantial cooperation in this
region. Where the model predicts low cooperation at this basin-size, the
evidence from Treatment $\left({}^{N=4}_{X=\$9}\right)$ pushes towards this
same conclusion, just in a starker way. Aside from the more-extreme
coordination effects at $\left({}^{N=4}_{X=\$9}\right)$, for the other three
treatments the theoretically standard extension of the strategic uncertainty
measure comes very close to _quantitatively_ predicting the ongoing
cooperation level using the out-of-sample relationship estimated from the two-
player RPD meta-data.

We summarize the main findings:

######  Result 1 (Independent-Basin Measure).

The independent-basin measure qualitatively organizes the results for ongoing
cooperation, and in all but one treatment matches the quantitative level
predictions. However, it does not contain all relevant information for
predicting initial intentions to collude.

######  Result 2 (Correlated-Basin Measure).

Our data is not consistent with the predictions from the correlated-basin
hypothesis, neither for initial, nor ongoing cooperation. In particular, where
the correlated basin predicts that behavior should ceteris paribus be
unaffected by $N$ we instead find large cooperation decreases with increases
to $N$.

##  5\. Extensions

Our analysis so far has abstracted away other features of the coordination
problem to focus on the pure effects from the primitives of the strategic
game. In this section we consider two extensions—with relevance both inside
and outside the laboratory—that allow us to study possible limitations of the
strategic-uncertainty model to predict changes in equilibrium selection.

First, we consider the extent to which beliefs on others’ collusive behavior
may be distorted by prior experience. While a policy change can change market
primitives and the strategic-uncertainty measure, the underlying variable in
this model is beliefs on others’ collusion. It seems plausible that beliefs
may be driven by experience before any change in the primitives, and so the
model may fare poorly at predicting changes within a population. For example,
if a player has engaged extensively with the _same_ population of market
participants under a status quo that led to non-collusive behavior, their
beliefs on others acting in this way may be sticky, and therefore unresponsive
to shifts in the primitives that have large effects in the strategic
uncertainty model. Our treatments in the previous section used a between-
subjects design. Identification relied on comparisons of late-session behavior
across different populations, each with experience under a fixed environment.
In a modified treatment pair we examine the effects of varying the number of
players $N$ within the same population, so that participants have experience
at two distinct values. In this extension we show that outcomes do not exhibit
long-run stickiness, where the between-subject results detailed previously are
not substantially dissimilar when we examine them within-subject.

In a second set of extensions, we examine the strategic uncertainty mechanism
underlying the basin-size selection device. In particular we examine the
extent to which our results are affected by the possibility of explicit
coordination, holding constant $X$ and $N$. Here we seek to mirror an
empirical finding that when collusion in industries is detected, it is often
accompanied by evidence of explicit collusion—despite the illegality of such
meetings.393939See Marshall and Marx (2012) for a more comprehensive
treatment. In one treatment we show that once explicit collusion is allowed
for, neither the independent nor the correlated basin measures does a good job
of predicting collusive behavior levels. Once parties can explicitly collude
we find very high levels of sustained cooperation. This suggests that indeed
uncertainty over the other strategic choices is a main driver of behavior in
our main treatments. However, the extremeness of the effect once communication
is allowed for raises a question over the extent to which explicit collusion
might lead to high cooperation rates even when collusive outcomes are not
equilibrium. To examine this, we show that there a clear limits on what
explicit collusion can achieve is defined by the theoretical existence of
collusive equilibria.

###  5.1. Between vs. Within Identification

The motivating idea for our first extension is that in many settings of
interest the policy-relevant comparative static is being varied within a
population. However, if agents have strong beliefs about others due to prior
experiences, it may be that our theoretical construction lacks bite at
predicting outcomes as the policy shifts. If selected equilibria are very
sticky within a population, then more-standard assumptions maintaining the
equilibria across the counterfactual may have greater validity. For example,
within the experiment if a participant’s experience with others is that they
play the stage-game defection action every period, then this belief can
persist despite a policy shift that makes collusion easier.

Ideally, we would introduce a primitive change within a supergame—for example,
a move from $N=4$ to $N=2$, where the matched player after the modification is
one of the matched participants from before. In exploring potential designs
for this, we were not satisfied that they would produce clear results. First,
it is well-documented that repeated-game environments require several
supergames of experience for participants to internalize the environment (Dal
Bó, 2005). While implementing a surprise change in $N$ as a mid-supergame
manipulation would mirror an outside-the-laboratory consolidation, this would
provide a single supergame observation, and require substantial explanation
across the surprise. An alternative design choice could implement a change in
$N$ with some probability within each supergame. However, any observed effects
would then be confounded with the expectations over the primitive change (and
greater complication in the instructions) and would no longer comparable to
our between-subject treatments.

Given the potential confounds with other designs we instead opted—certainly as
a first approach— for a design with a surprise one-time shift in the number of
players $N$, but where this occurred in a fixed session-level population.
Holding constant the cooperation cost at $X=\$9$, we initially set a value of
$N$ (either two or four) for the first ten supergames. We then change the
value of $N$ for the last ten supergames (to either four or two,
respectively).

This led to two further experimental treatments, one with
$\left({}^{N=2}_{X=\$9}\right)$ in the first half, and
$\left({}^{N=4}_{X=\$9}\right)$ in the second; and the converse treatment from
$\left({}^{N=4}_{X=\$9}\right)$ in the first, to
$\left({}^{N=2}_{X=\$9}\right)$ in the second half. In both treatments, the
change in $N$ comes as a surprise: subjects know there is a second part, but
do not receive instructions on it until supergame ten concludes.404040Our
between-subject treatments also divided the session into two parts, except
that once subjects reached the second half of the session they were told that
part two was identical to part one. In terms of the standard strategic-
uncertainty model this creates a shift across the session from a low basin-
size of 0.33 when $N=2$, and a high basin-size of 0.69 when $N=4$. In
particular, this is a change in $N$ where our between-subject design indicates
a substantial treatment effect. Given that we hold constant $X=\$9$, for
simplicity we label the treatments as $2\rightarrow 4$ and $4\rightarrow 2$,
for the first-half to second-half shifts.

In Figure 3(A) we present the average initial cooperation-rates across the
session’s twenty supergames. The between-subject treatments with $N=2$ and
$N=4$ are indicated by the two gray dashed lines (separately labeled), while
the within-subject treatment results are represented by two black lines: a
solid line for the $2\rightarrow 4$ treatment, and a dash-dotted-line for the
$4\rightarrow 2$ treatment. The figure illustrates the substantial between-
subject effect, with more cooperation in $\left({}^{X=\$9}_{N=2}\right)$ over
$\left({}^{X=\$9}_{N=4}\right)$ for all twenty supergames. Our within and
between sessions are identical for the first ten supergames, where the figure
indicates replicated effects. Pooling the between and within treatments with
$N=2$ in supergames 6–10 the initial cooperation rate is 47.4 percent. In
contrast, the pooled cooperation rate for $N=4$ is just 13.9
percent.414141Testing the initial cooperation rate differences in supergames
6–10 over $N$ (so across the between and within sessions with identical
treatment at this point) we find $p=0.150$ for $N=2$ and $p=0.981$ for $N=4$
from $t$-tests for a level difference, and $p=0.353$ for a joint test.

As we move into supergames 11–20, the number of players matched in each
supergame changes for our within treatments. Figure 3(A) indicates the
immediate shift in behavior as the primitive changes as the two vertical
dotted lines. For the $2\rightarrow 4$ treatment (the black solid line)
initial cooperation levels remain fairly high after the shift from $N=2$ to
$N=4$. In fact, cooperation in the first four-player interaction (supergame
11) actually exhibits an increase to 59.7 percent from the 53.0 percent from
the last two-player interaction (supergame 10). However, while there is no
immediate cooperation drop-off, and thus stickiness, as subjects gain
experience at $N=4$ the cooperation rate falls rapidly, reaching 16.7 percent
by supergame 20. In contrast, moving in the other direction from $N=4$ to
$N=2$ (the black dash-dot line) we find an immediate jump with the primitive
shift. Where initial-round cooperation in supergame 10 with four-players is
18.3 percent, the reduction to $N=2$ pushes this rate up to 60.0 percent for
supergame 11. The immediate jump in behavior is then sustained across the
remaining supergames, with 58.3 percent cooperation in supergame 20.

Inspecting the session time-series illustrated in Figure 3(A) it is clear that
the there is little evidence for the hypothesis that equilibrium selection is
sticky in the long-run under a within-population shift in $N$. Despite
exposure to the alternative environment in the first half, longer-run behavior
in the second-half is not substantially dissimilar from the between-subject
levels. This is indicated by the close proximity of the two black/gray line
pairs at supergame 20, and relative distance from the other pair.

(a) Between vs. Within ($X=\$9$) (b) Explicit vs. Implicit
($\left({}^{N=4}_{X=\$9}\right)$)

Figure 3. Initial cooperation rates in extensions (by supergame)

In Online Appendix B we provide a more detailed like-with-like comparison of
the between-subject and within-subject results. These more-detailed findings
indicate no difference with the between-subject results as we move from
$2\rightarrow 4$. However, in opposition to the hypothesis that the selected
equilibrium is sticky, we actually find a significant _increases_ in the
response to $N$ over the between analysis as we move from $4\rightarrow 2$. We
summarize the result:

######  Result 3 (Between vs. Within).

Switching the identification to within does not substantially change our
qualitative results, finding no evidence that the selected equilibrium is
sticky in the long run as we shift a primitive within the population. If
anything, our within-subject identification shows a larger shift than the
between-subject results as we decrease $N$.

###  5.2. Explicit Correlation

The focus so far, and for the RPD literature more generally, is an examination
of _implicit_ coordination. Our results thus far suggest that a model of
strategic uncertainty extended via independence is relatively successful at
organizing the data. This is particularly so for ongoing cooperation. In
contrast, a measure based on perfectly correlated play fails to predict the
substantial effect of $N$ for both initial and ongoing behavior.

These results are therefore a validation of a standard extension of the basin
of attraction notion. However, correlation across participants’ beliefs
becomes much more plausible when participants have access to a channel through
which to explicitly coordinate. In an extension to our previous experiments we
now examine the extent to which multiple parties successfully collude when
given a coordination device.

To this end, we designed a further treatment pair that modifies our
environment with the starkest coordination on the non-collusive outcome, the
$\left({}^{N=4}_{X=\$9}\right)$ treatment. In the first chat treatment, the
first 10 supergames were identical to the $\left({}^{N=4}_{X=\$9}\right)$
treatment, but we introduce pre-supergame chat between the four matched
players in supergames 11–20. A second chat treatment is identical to the first
in terms of the timing for when we introduce the chat coordination device; the
difference is that we reduce the continuation probability to
$\delta^{\prime}=\nicefrac{{1}}{{2}}$ for the entire session. The designed
effect of this change is that while the stage-game payoffs and number of
players is held constant, at this value of $\delta$ the grim trigger is now
only a knife-edge SPE, where the critical belief
$p^{\star}(\delta^{\prime})=1$ under both (2) and (3). The
$\delta=\tfrac{1}{2}$ treatment therefore serves as a test for whether
explicit coordination can implement outcomes that are not supportable as a
robust equilibrium (that is, with arbitrarily small trembles in behavior).

Table 3. Cooperation: Implicit vs. Explicit

| Implicit |  | Explicit
---|---|---|---
| $\text{NoChat}(\nicefrac{{3}}{{4}})$ |  | $\text{Chat}(\nicefrac{{3}}{{4}})$ | $\text{Chat}(\nicefrac{{1}}{{2}})$
Initial coop. | $\underset{\mbox{{\tiny$\left(0.017\right)$}}}{0.035}$ |  | $\underset{\mbox{{\tiny$\left(0.007\right)$}}}{0.988}$ | $\underset{\mbox{{\tiny$\left(0.037\right)$}}}{0.300}$
Ongoing coop. | $\underset{\mbox{{\tiny$\left(0.003\right)$}}}{0.006}$ |  | $\underset{\mbox{{\tiny$\left(0.030\right)$}}}{0.806}$ | $\underset{\mbox{{\tiny$\left(0.018\right)$}}}{0.044}$
Initial success | 0.000 |  | 0.971 | 0.094
Ongoing success | 0.000 |  | 0.756 | 0.002

Note: All treatments have $x=\$9,N=4$, where
$\text{NoChat}(\nicefrac{{3}}{{4}})$ is from the core $2\times 2$ between-
subject design outline in section 4. Data taken from last five supergames,
participant-clustered standard errors in parentheses.

In an online supplement we provide chat logs for the interested reader;
however, we here focus on the of effects of chat on cooperation levels. In
Figure 3(B) we plot the average initial cooperation rates across sessions
(with the $\left({}^{N=4}_{x=\$9}\right)$ treatment provided as a baseline,
labeled here as NoChat($\nicefrac{{3}}{{4}}$)). Late-session cooperation and
success rates (assessed in supergames 16–20 with subject-clustered standard
errors) are provided in Table 3.

Our first chat treatment delivers unequivocal results: providing pre-play
communication at $\delta=\nicefrac{{3}}{{4}}$ takes the near-zero cooperation
rate in the absence of chat to almost complete cooperation. While ongoing
cooperation drops slightly from the very high initial-cooperation levels, the
large majority of supergames exhibit coordination by all four participants on
the efficient/collusive outcome. Such high levels of cooperation with
communication are inconsistent with the predictions of either model of
equilibrium selection for these primitives. This suggests that once explicit
coordination devices are allowed for and strategic uncertainty is reduced, the
independent model–that captured behavior when collusion is tacit–is no longer
helpful.

However, at the $\delta=\nicefrac{{1}}{{2}}$ boundary for dynamic strategies
to be incentive compatible, even with pre-play communication participants find
it hard to coordinate. While initial cooperation levels are substantially
higher than the treatment without chat at 30.0 percent, ongoing cooperation
falls to just 4.4 percent, where successful joint-cooperation across an entire
group in an ongoing round becomes exceedingly rare at 0.2 percent. The
findings therefore indicate that for explicit communication to play a role,
clear incentives for collusion do need to be present.

Given the very stark findings here, we simply summarize the extension result:

######  Result 4 (Implicit vs. Explicit).

Explicit coordination leads to very high cooperation levels with multiple
players, in a setting where implicit cooperation achieves near-zero
cooperation. However, in the limiting case, where cooperation is a knife-edge
SPE outcome, even pre-play chat fails to support cooperation in our
experiments.

##  6\. Conclusion

Our paper examines equilibrium selection in repeated games, and the extent to
which it can be predicted with a model of strategic uncertainty. We leverage a
model of equilibrium selection that rationalizes behavior in data from
repeated prisoner’s dilemma (RPD) experiments and design an experiment to
stress test this specific theoretical model. The predictive model works by
mediating the effects from multiple-primitives into a single dimension,
strategic uncertainty. As such, even for rich counterfactual policies with
many changes to the setting, the model can still generate a directional
prediction. The experimental design builds on this motivation for the model,
introducing a novel source of strategic uncertainty that has not been studied
in the RPD setting (the number of players) while also manipulating a payoff
parameter. We can thus change both sources of strategic uncertainty
simultaneously and study the extent to which the evidence is consistent with
the predictions of the selection model. Our main finding is that the model of
equilibrium selection can indeed be used as a device for understanding
successful coordination on the collusive outcome. In particular, the model
performs well in trading-off the competing effects from the two distinct
sources of strategic uncertainty.

After illustrating the theoretical power of the model for implicit
coordination, we turn our attention to two application-motivated extensions
that probe its limitations. In the first, we are motivated by the extent to
which prior history and experience could make the equilibria “sticky,” even
where the model suggests a change. To do this, we study the extent to which
our findings still hold when treatment-variable manipulations takes place
within the same population, as opposed to between populations in our main
study. The results indicate that eve when the participants experience a
treatment-variable shift, the model still continues to predict the longer run
outcomes. While we do find some hysteresis in the short-run response to a
within-population policy change—initial stickiness in behavior in one
direction and a large immediate response to the change in the other—behavior
after some experience under the new parameters is not distinct from the
between-population treatments. As such, while a plausible limitation of the
model was the effect of prior experience, these results suggest that the model
prediction fares better than the more-standard assumption of maintaining a
selected equilibrium across a policy change.

Finally, in a second extension, we examine the potential effects from explicit
collusion. Shifting the experimental environment by providing an explicit
coordination device (pre-play chat) we examine a necessary limitation on the
model if the underlying strategic uncertainty mechanism is correct. Our main
finding here is that once we allow for explicit coordination then the
selection-model prediction is very far from observed behavior. In fact, where
the model suggests very low levels of cooperation, actual behavior is at the
other extreme once coordination devices are present. The evidence from the
second extension therefore indicates both that strategic uncertainty plays a
clear role, but also that the selection model based upon it is entirely
inappropriate for predicting behavior when explicit collusion is suspected.

Though our results are encouraging, for the theoretical selection model we
examine to be useful in applications further tests are needed. First, as we
point out when describing our experimental design, there are many ways in
which expanding the multiple players might impact the game.Because we do not
want to introduce further coordination issues, we focus on a setting where
collusion requires joint cooperation form all of the agents. But in other
interesting environments cooperation among a subset of the agents may be
enough for reaching an efficient outcome. Such environments introduce further
distributional coordination problems, over who cooperates and who free-rides.
Further research is needed to evaluate how and if models of equilibrium
selection might be extended to such problems. Outside from the role of
multiple players, there are also outstanding questions with regard to how
asymmetries for the players—in terms of actions, payoffs, and the
sequentiality of moves—should be modeled.

From another perspective, our results also outline that there is room to
evaluate the role for equilibrium selection model in environments with
explicit collusion. Our findings suggest one clear limit on where explicit
collusion can play a role: the existence of a collusive equilibrium. However,
beyond this point, not much is known about the conditions for which explicit
communication between the parties is enough for collusion. Another direction
for future research is to try to understand if there are ways to manipulate
the primitives to understand when explicit collusion will and will not be
successful.

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##  Appendix A Additional Tables and Figures

Table A.1. Cooperation rates (All supergames)

Cooperation rates | $x=\$9$ |  | $x=\$1$
---|---|---|---
$N=2$ | $N=4$ |  | $N=4$ | $N=10$
Initial coop. | $\underset{\mbox{{\tiny$\left(0.046\right)$}}}{0.466}$ | $\underset{\mbox{{\tiny$\left(0.021\right)$}}}{0.100}$ |  | $\underset{\mbox{{\tiny$\left(0.039\right)$}}}{0.719}$ | $\underset{\mbox{{\tiny$\left(0.044\right)$}}}{0.457}$
Ongoing coop. | $\underset{\mbox{{\tiny$\left(0.029\right)$}}}{0.296}$ | $\underset{\mbox{{\tiny$\left(0.012\right)$}}}{0.044}$ |  | $\underset{\mbox{{\tiny$\left(0.034\right)$}}}{0.433}$ | $\underset{\mbox{{\tiny$\left(0.039\right)$}}}{0.243}$
Initial success | 0.466 | 0.003 |  | 0.408 | 0.010
Ongoing success | 0.296 | 0.002 |  | 0.275 | 0.009

Note: Results are calculated using data from all supergames. Cooperation rates
present raw proportions (with subject-clustered standard errors).

Table A.2. Cooperation in reaction to previous round’s history

| $x=\$9$ |  | $x=\$1$ |  | Chat ($x=\$9,N=4$)
---|---|---|---|---|---
History | $N=2$ | $N=4$ |  | $N=4$ | $N=10$ |  | $\delta=\nicefrac{{3}}{{4}}$ | $\delta=\nicefrac{{1}}{{2}}$
$(C,S)$ | $\underset{\mbox{{\tiny$\left(0.011\right)$}}}{0.977}$ | – |  | $\underset{\mbox{{\tiny$\left(0.013\right)$}}}{0.988}$ | – |  | $\underset{\mbox{{\tiny$\left(0.006\right)$}}}{0.980}$ | $\underset{\mbox{{\tiny$\left(0.217\right)$}}}{0.750}$
$(C,F)$ | $\underset{\mbox{{\tiny$\left(0.063\right)$}}}{0.317}$ | $0.000$ |  | $\underset{\mbox{{\tiny$\left(0.085\right)$}}}{0.521}$ | $\underset{\mbox{{\tiny$\left(0.077\right)$}}}{0.739}$ |  | $\underset{\mbox{{\tiny$\left(0.0073\right)$}}}{0.342}$ | $\underset{\mbox{{\tiny$\left(0.104\right)$}}}{0.255}$
$(D,S)$ | $\underset{\mbox{{\tiny$\left(0.060\right)$}}}{0.150}$ | – |  | $\underset{\mbox{{\tiny$\left(0.110\right)$}}}{0.263}$ | – |  | $\underset{\mbox{{\tiny$\left(0.136\right)$}}}{0.143}$ | $\underset{\mbox{{\tiny$\left(0.217\right)$}}}{0.750}$
$(D,F)$ | $\underset{\mbox{{\tiny$\left(0.006\right)$}}}{0.033}$ | $\underset{\mbox{{\tiny$\left(0.004\right)$}}}{0.006}$ |  | $\underset{\mbox{{\tiny$\left(0.009\right)$}}}{0.023}$ | $\underset{\mbox{{\tiny$\left(0.009\right)$}}}{0.025}$ |  | $\underset{\mbox{{\tiny$\left(0.019\right)$}}}{0.019}$ | $\underset{\mbox{{\tiny$\left(0.004\right)$}}}{0.006}$

Note: Data taken from last five supergames in each treatment (with subject-
clustered standard errors). Cells marked “–” have no observations at the
relevant history. History shows the own-action-signal pair from the previous
round, $(a_{t-1},\sigma_{t-1})$.

(a) Initial cooperation (b) Ongoing cooperation

Figure A.1. Cooperation and the Correlated Basin-Size Model

Note: Figures show pooled data by the correlated basin (diamonds) while the
separate treatments are illustrated as the surrounding circles. See Figure 2
in the main paper for the analogous figure under the independent basin.

##  Appendix B Further Analysis of the Within-Subject Treatments

We do find evidence that is hysteresis in the dynamics though. A large and
immediate jump in cooperation is observed as the game moves from $N=4$ to
$N=2$, but with no initial response when $N$ moves in the opposite direction.
This suggests that in the short run, absent experience with the new
environment subjects are likely to try to coordinate on cooperation. Notice,
however, that the response to the change in $N$ in the initial supergames of
the second half can be compared against the initial supergames of the first
half. Shifting the illustrated behavior for supergames 11–20 in Figure 3(A)
ten supergames to the left and comparing the observed levels to supergames
1–10 makes the jump patterns less clear. In the first ten supergames under
$N=4$ the pattern is very similar: cooperation is initially high, but it falls
rapidly as the subjects gain experience. Similarly for the $N=2$ trend.

While some caution is warranted as the qualitative trends as they gain
experience under the new parameterization are similar to the initial trends
with no prior experience, direct comparisons of behavior in supergames one and
eleven do reject equivalence. With no experience at all in the environment,
43.2 percent of subjects cooperate for $N=2$ in the first round of the first
supergame, compared to 29.4 percent for $N=4$ (significantly different with
$p=0.005$ from a test of proportions). In contrast to the significant
difference over $N$ in the very first decision, in supergame 11 of our within-
subject sessions (with prior experience at an alternate value of $N$) the
initial cooperation rates at $N=2$ and $N=4$ can not be distinguished from one
another in the plotted figure (at 60.0 and 59.7 percent cooperation,
respectively), let alone statistically ($p=0.974$). Both cooperation rates are
significantly greater than the initial responses in supergame one.424242Given
the disjoint subject groups and identical treatment in supergames 1–10, we
compare proportions using $t$-tests without clustering. We then compare the
initial response under each value of $N$ in the within-subject supergame
eleven to all subjects at that $N$ in supergame one. Using these tests we
reject equivalence with $p=0.021$ for $N=2$ and $p<0.001$ for $N=4$. We
conclude that experience at another parameter value in the first half does
cause both treatments’ cooperation rates to increase.

Table A.3. Cooperation: Between vs. Within

| Between (SG 6–10) |  | Within (SG 16–20) | $\Delta_{\text{Btwn.}}$ | $\Delta_{\text{Wthn.}}$
---|---|---|---|---|---
| $N=2$ | $N=4$ |  | $N=2$ | $N=4$ |  | $2\rightarrow 4$ | $4\rightarrow 2$
Initial coop. | $\underset{\mbox{{\tiny$\left(0.036\right)$}}}{0.474}$ | $\underset{\mbox{{\tiny$\left(0.025\right)$}}}{0.139}$ |  | $\underset{\mbox{{\tiny$\left(0.056\right)$}}}{0.643}$ | $\underset{\mbox{{\tiny$\left(0.041\right)$}}}{0.214}$ | $\underset{\mbox{{\tiny$\left(0.060\right)$}}}{-0.469}$ | $\underset{\mbox{{\tiny$\left(0.042\right)$}}}{-0.260}$ | $\underset{\mbox{{\tiny$\left(0.056\right)$}}}{-0.504}$
Ongoing coop. | $\underset{\mbox{{\tiny$\left(0.026\right)$}}}{0.299}$ | $\underset{\mbox{{\tiny$\left(0.012\right)$}}}{0.054}$ |  | $\underset{\mbox{{\tiny$\left(0.051\right)$}}}{0.598}$ | $\underset{\mbox{{\tiny$\left(0.016\right)$}}}{0.042}$ | $\underset{\mbox{{\tiny$\left(0.055\right)$}}}{-0.444}$ | $\underset{\mbox{{\tiny$\left(0.029\right)$}}}{-0.258}$ | $\underset{\mbox{{\tiny$\left(0.050\right)$}}}{-0.544}$
Initial success | 0.474 | 0.011 |  | 0.643 | 0.042 | -0.503 | -0.433 | -0.632
Ongoing success | 0.299 | 0.004 |  | 0.598 | 0.008 | -0.450 | -0.292 | -0.594

Note: Comparisons at the same experience level are generated using supergames
6–10 across all sessions (fixing $N$, between and within sessions are
identical until supergame 11). For the within change we measure the
cooperation rates in supergames 16–20. All cooperation rates are raw
proportions (with subject-clustered standard errors). The last three columns
measure the corresponding cooperation rate when $N=4$ minus the cooperation
rate when $N=2$.

In Table A.3 we provide more details, where we compare and contrast the
behavior after 5 rounds of experience. In the first two data columns we
present average behavior (initial/ongoing cooperation and success, with
subject-clustered standard errors for the individual choices) in supergames
6–10 for $N=2$, $N=4$. In the next column pair we present the same information
in supergames 16–20 for the within treatments only. Examining the differences
across the _within_ and _between_ cooperation levels, while we find no
significant differences in behavior for $N=4$ ($p=0.117/p=0.539$ for
initial/ongoing cooperation) we do find significant differences across the
$N=2$ cooperation rates ($p=0.011$ for initial, $p<0.001$ for ongoing). The
significant differences here reflect the substantially greater upward shift in
the $4\rightarrow 2$ treatment.

In the final three columns, we compute (for three different cases) the average
cooperation rate in supergames when $N=4$ minus the cooperation rate when
$N=2$. In the first column ($\Delta_{\text{Btwn}}$) we calculate the between-
subject change using data from supergames 16–20 in the $X=\$9$ between-subject
treatments. The results here are analogous to the marginal effect attributable
to an increase in the independent basin of $\Delta
p^{\star}_{\text{Ind.}}=+0.36$ in Table 2 once we remove the $X=\$1$
treatments. In the final column pair we present the same assessed treatment
effect if we used the within-subject difference in the $2\rightarrow 4$ and
$4\rightarrow 2$ treatments (here we compare data in supergames 6–10 to
supergames 16–20).

While the three measures agree qualitatively—and exhibit economically large
effects in $N$ in the same direction—there are differences, particularly in
the comparisons to the $2\rightarrow 4$ case. However, we note that there are
two effects at play here. In the $2\rightarrow 4$ comparison, reduced
magnitudes are driven primarily by the fact that behavior in this treatment
has not converged. To see this, consider the assessed between-subject effect
if we used data from supergames 6–10: a -33.5 percentage point effect on
initial cooperation, which is not significantly different from the -26.0
percent effect identified in the within comparison ($p=0.117$).434343Similarly
for ongoing cooperation the between-effect assessed in supergames 6–10 is
-24.6 percent compared to -25.8 percent within ($p=0.539$). In contrast, the
greater assessed effect in the $4\rightarrow 2$ comparison is the composite of
the same _reduction_ in the effect from looking at the still-converging data
for $N=4$, with a substantial increase in cooperation at $N=2$ in the second
half over the between-subject levels.

(a) Between vs. Within ($x=\$9$) (b) Explicit vs. Implicit ($N=4;x=\$9$)

Figure A.2. Initial success rates in extensions (by supergame)

##  Appendix C Interface Screenshots

(a) Action Selection

(b) Round Feedback

(c) Supergame Feedback

Figure A.3. Interface Screenshots

##  Appendix D Provided Instructions

Below we include the instructions given to participants. All language
deltas/treatment-specific language are included in braces. Text in red is for
the $N=2$ treatment, in blue for the $N>2$ treatments (here we provide the
$N=4$ implementation, where $N=10$ has only minor changes.). In green we
provide the payoff text for $X=\$9$, in orange for $X=\$1$. Separate
instructions for {Part two} are given by treatment for the extensions. The
only unlisted treatment variation here is for the Chat($\nicefrac{{1}}{{2}}$)
treatment, where the only changes are for the critical die rolls in the _Study
Organization & Payment_ section, where the supergame cutoff changes from 75 to
50.

## Instructions

### Welcome

You are about to participate in a study on decision-making. What you earn
depends on your decisions, and the decisions of others in this room. Please
turn off your cell phones and any similar devices now. Please do not talk or
in any way try to communicate with other participants. We will start with a
brief instruction period. During the instruction period you will be given a
description of the main features of the study. If you have any questions
during this period, raise your hand and your question will be answered in
private at your computer carrel.

### Study Organization & Payment

  * •

The study has two Parts, where each Part has 10 decision-making Cycles. Each
Cycle consists of a random number of Rounds where you make decisions.

  * •

At the end of the study, one of the two Parts will be selected for payment
with equal probability. For the selected Part, one of the 10 Cycles will be
randomly selected for payment. Your payment for this randomly selected Cycle
will be based on your decision’s in that Cycle’s last Round.

  * •

The number of Rounds in each Cycle is random, where only the last Round in
each Cycle counts for payment. Which Round is the last is determined as
follows:

    * –

In every Round, after participants make their decisions, the computer will
roll a fair 100-sided die. If the die roll is greater than 75 (so 76–100) the
round just completed is the one that is used to determine the current Cycle’s
payment, and the Cycle ends. If instead the computer’s roll is less than 75
(so 1– 75) then the Cycle continues into another Round.

    * –

Because of this rule, after every Round decision there is a 25 percent chance
that the current Round is the ones that count for the Cycle’s payment, and a
75 percent chance that the Cycle continues and the decisions in a subsequent
round will count for that Cycle payment.

  * •

Your final payment for the study will be made up of a $6 show-up fee, and your
payment from the last Round in the randomly selected Cycle.

### Part 1

  * •

In the first part of the study you will make decisions in 10 Cycles. In each
Cycle you will be matched with {another participant}{a group of three other
participants} in the room for a sequence of Rounds. You will interact with the
same {other participant}{group of three other participants} in all rounds of
the cycle.

  * •

Once a Cycle is completed, you will be randomly matched to a new
{participant}{group of three participants} for the next Cycle.

  * •

While the specific {participant}{participants} you are matched to is fixed
across all Rounds in the Cycle, the computer interface in which you make your
decisions is anonymous, so you will never find out which participants in the
room you interacted with in a particular Cycle, nor will others be able to
find out that they interacted with you.

### Round Choices and Payoffs

For each Round in each Cycle, you and the matched {participant}{participants
in your group} will make simultaneous choices. {Both}{All four} of you must
choose between either the Green action or the Red action. After you and the
other {participant}{three participants} have made your choices, you will be
given feedback on the {other participant’s}{other participants’} choices that
Round, alongside the Computer’s die roll to determine if that Round counts for
the Cycle payment.

If a particular Round is the Cycle’s last, and that Cycle is the one selected
for final payment, there are four possible payoff outcomes.

  1. (i)

If both you and {the other participant}{all three of the other participants}
choose the Green action, you get a round payoff of $20.

  2. (ii)

If you choose the Green action and {the other participant chooses}{any of the
other participants choose} Red, you get a round payoff of {$2}{$10}.

  3. (iii)

If you choose the Red action and {the other participant chooses}{all of the
three other participants choose} Green, you get a round payoff of {$29}{$21}.

  4. (iv)

If both you and {the other participant}{any of the other three participants}
choose the Red action, you get a round payoff of $11.

These four payoffs are summarized in the following table:

|  | Other {Participant’s Action:}{Participants’ Actions:}
---|---|---
|  |  {Green}{All 3 Green} |  {Red}{Any of 3 Red}
Your Action: | Green | $20 | {$2}{$10}
Red | {$29}{$21} | $11

Some examples of these payoffs:

Case 1. Suppose you choose Green and {the other participant}{all three of the
other participants} in the Cycle also choose Green. If that Round is the final
one in the Cycle {both}{all four} of you would get a payoff of $20.

Case 2. Suppose {you}{you and two of the other participants} choose Green
while the other participant chooses Red. If that Round is the final one in the
Cycle {you}{you and the other two participants who chose Green} would get a
payoff of {$2}{$10}, while the other participant would get a payoff of
{$29}{$21}.

Case 3. Suppose you chooseRed while {the other participant chooses}{all three
of the other participants choose} Green. If that Round is the final one in the
Cycle you would get a payoff of {$29}{$21}, while the other
{participant}{three participants} would get a payoff of {$2}{$10}.

Case 4. Suppose you and {the other participant choose Red.}{another
participant choose Red while the other two participants choose Green.} If that
Round is the final one in the Cycle {you}{you and the other participant that
chose Red} would get a payoff of {$11}{$11, while the other two participants
would get a payoff of{$2}{$10}} .

### Part 2

After Part 1 is concluded, you will be given instructions on Part 2, which
will have a very similar structure to the task in Part 1.

{END OF PART 1 HANDOUT}

### Part 2 Instructions {Between Only, handed out Supergame 11}

Part 2 is identical to Part 1. In each of the 10 Cycles in Part 2 you will
again be matched to {another participant}{three other participants} in the
room.

Similar to Part 1, the Cycle payoff is determined by the last round in the
Cycle, where the payoff depends on the action you chose and the {action chosen
by the matched participant}{actions chosen by the three matched participants}
for that Cycle. Similar to Part 1, the below Table summarizes the payoff based
upon the choices made in the Cycle’s last round.

|  | Other {Participant’s Action:}{Participants’ Actions:}
---|---|---
|  |  {Green}{All 3 Green} |  {Red}{Any of 3 Red}
Your Action: | Green | $20 | {$2}{$10}
Red | {$29}{$21} | $11

{END OF PART 2 HANDOUT}

### Part 2 Instructions {Within Only, handed out Supergame 11}

Part 2 is very similar to Part 1. However, in each of the 10 Cycles in Part 2
you will instead be matched to three other participants in the room for each
Cycle.

Similar to Part 1, the Cycle payoff is determined by the last round in the
Cycle, where the payoff depends on the action you chose and the actions chosen
by the three matched participants for that Cycle. If a particular Round is the
Cycle’s last, and that Cycle is the one selected for final payment, there are
four possible payoff outcomes.

  1. (i)

If both you and all three of the other participants choose the Green action,
you get a round payoff of $20.

  2. (ii)

If you choose the Green action and any of the other participants chooses Red,
you get a round payoff of $2.

  3. (iii)

If you choose the Red action and all three other participants choose Green,
you get a round payoff of $29.

  4. (iv)

If both you and any of the other three participants choose the Red action, you
get a round payoff of $11.

These four payoffs are summarized in the following table:

|  | Other Participant’s Action:
---|---|---
|  | All 3 Green | Any of 3 Red
Your Action: | Green | $20 | $2
Red | $29 | $11

Some examples of these payoffs:

Case 1. Suppose you choose Green and all three of the other participants in
the Cycle also choose Green. If that Round is the final one in the Cycle all
four of you would get a payoff of $20.

Case 2. Suppose you and two of the other participants choose Green while the
other participant chooses Red. If that Round is the final one in the Cycle you
and the other two participants who chose Green would get a payoff of $2, while
the other participant would get a payoff of $29.

Case 3. Suppose you choose Red while all three of the other participants
choose Green. If that Round is the final one in the Cycle you would get a
payoff of $29, while the other three participants would get a Round payoff of
$2.

Case 4. Suppose you and another participant choose Red while the other two
participants choose Green. If that Round is the final one in the Cycle you and
the other participant that chose Red would get a payoff of $11, while the
other two participants would get a payoff of $2.

{END OF PART 2 HANDOUT}

### Part 2 Instructions {Chat Only, handed out Supergame 11}

Part 2 is identical to Part 1 except for the beginning of each cycle where we
will now allow the matched participants to chat to one another before the
cycle begins. In each of the 10 Cycles in Part 2 you will again be matched to
three other participants in the room.

Similar to Part 1, the Cycle payoff is determined by the last round in the
Cycle, where the payoff depends on the action you chose and the actions chosen
by the three matched participants for that Cycle. Similar to Part 1, the below
Table summarizes the payoff based upon the choices made in the Cycle’s last
round.

|  | Other Participants’ Actions:
---|---|---
|  | All 3 Green | Any of 3 Red
Your Action: | Green | $20 | $2
Red | $29 | $11

In contrast to Part 1 though, at the beginning of each new cycle, a chat
window will be given to you, which will stay open for two minutes, or until
all group members close it.

You may not use the chat to discuss details about your previous earnings, nor
are you to provide any details that may help other participants in this room
identify you. This is important to the validity of this study and will be not
tolerated. However, you are encouraged to use the chat window to discuss the
upcoming Cycle.

If at any point within the two-minute limit you wish to leave the chat, you
can click the “Finish Chat” button. The other participants will be informed
that you left.

{END OF PART 2 HANDOUT}