Allowing for Cheap Talk
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Can Cheap Talk Help Build Reputations? An Experimental Analysis
Dustin Tingley1 Politics Department, Princeton University
Barbara Walter Political Science Department, UCSD Abstract
What effect does cheap talk have on behavior in an environment where subjects have an incentive to build reputations? We shed light on this question by using incentivized laboratory experiments of strategic interaction. Our results suggest that cheap talk can have a substantial impact on behavior. In particular, we observe that players regularly sent threats to their opponents, were more likely to back those threats up with fighting, and were able to deter opponents in early periods of play. We believe these results bring fresh new evidence to the field of international relations about the importance of cheap talk.
1 Work in progress. We are especially thankful to Anne Sartori and Kristopher Ramsay for discussions, and Ernesto Ruben for help programming our software interface. In most bargaining models, verbal threats or promises about future actions are modeled as cheap talk and are not expected to affect behavior in all but relatively specific situations. In practice, however, leaders engage in cheap talk all the time. During the
Cuban Missile Crisis, for example, President Kennedy gave a verbal promise to Soviet
Premier Nikita Khrushchev to remove American nuclear missiles from Turkey and this promise appeared to help resolve the crisis.
The fact that leaders rely on costless statements is puzzling. If verbal promises and threats are not worth the paper they are written on, as Yogi Berra once stated, why would so many leaders bother to use them? And why would the targets of these promises and threats ever believe them?
In what follows, we believe that the role of costless, non-verifiable communication in bargaining is more important than much of the international relations literature has given it credit for. This is not the case in economics, where a number of scholars have studied the value of cheap talk. Vince Crawford, a pioneer in the economic analysis of cheap talk, for example, notes that “(l)ying for strategic advantage about planned actions, or intentions, is a common feature of economic and political as well as military life” (2003, pg. 133). Similarly, Farrel and Gibbons observed that “[t]alk is ubiquitous and is often listened to, even where no real penalty attaches to lying, and where claims do not directly affect payoffs” (1989, pg. 222). Verbal claims about one’s intentions may be costless, but they do appear, at times, to work.
In what follows we show, using a laboratory experiment, that cheap talk can effectively deter a challenge even in situations where the credibility of a verbal threat cannot be verified. In a simple laboratory experiment we compare how defenders and challengers in an entry deterrence game - a repeated bargaining situation with incomplete information - behave when costless threats are possible and when they are not. We have two goals with this experiment. The first is to see when and how cheap talk is used. If parties have the option of sending a verbal threat, how often and under what conditions do they choose to do this? The second goal is to see what effect, if any, cheap talk has.
Once a threat has been issued, does it have any effect on the behavior of the target, or are senders required to take more costly action in order to deter entry?
We use incentivized laboratory experiments to study these questions. Alternative research approaches certainly can help us understand the role of cheap talk (e.g., (Sartori
2005)). However, we feel that there are several reasons laboratory experiments might be a particularly helpful tool. First, any non-laboratory study of cheap talk faces a potentially serious selection problem because cases where cheap talk has worked are difficult to observe. Threats that are effective, for example, generally convince the target not to act. In the laboratory, by contrast, we are able to directly observe all decisions, even those that result in a subject taking no action at all. Second, studies outside the laboratory also have difficulty determining what types of communication count as cheap talk. In the laboratory, we can directly examine only those types of communication that have no direct bearing on player utilities. Laboratory experiments, therefore, represent a unique resource for uncovering the specific causal effects of this particular phenomenon.2
Our experiments reveal three unexpected patterns. When given the opportunity, individuals choose to send verbal threats most of the time despite the fact that they are known to be costless. We also find that individuals are significantly more likely to act on
2 Of course, we understand that laboratory experiments come with their own host of problems, and thus see these experiments as fitting into a broader, multi-method, research approach to the question. these threats once they had been made even though there are no punishments for not following through. And finally, targets are more likely to back down in the face of a threat notwithstanding the inherent weakness of these threats. In short, individuals engaged in cheap talk far more than we expected, and it often had the desired effect.
The remainder of the paper is broken down into four sections. In the first section we discuss existing explanations in the economics literature for when cheap talk is likely to be effective and when it is not. We also review existing empirical studies in order to situate our experiment. In section two we introduce our experimental design, discuss some theoretical predictions, and explain our empirical strategy. Section three presents the results of the experiments and discusses what this tells us more generally about the strategic use of communication and why cheap talk continues to be used even though most rational choice models say it should not. In the final section we conclude.
What We Know Theoretically About Cheap Talk
Verbal communication has been viewed as ineffective because much of it is costless. Leaders can threaten or promise to take action, but unless lying can be punished, such communication cannot distinguish between leaders who are sincere and those who are not.3
Still the ubiquity of cheap talk in the real world has attracted the attention of a number of formal theorists and at least five equilibrium models have been developed to suggest why it may still occur. The first model, developed by Crawford and Sobel,
3 Conversely, costly signaling is often taken to be informative. For example, in Spence type models of signaling, communication is about a player’s “type”, where type relates to some feature of the player like their payoffs. By making signals costly, senders are effectively able to separate themselves from other player types and recipients are able to partition the set of actors they face into sets of players sharing a common type. Of course, costly signaling does not guarantee that this separation will occur, but only that there often exist equilibria where this does happen. shows that cheap talk can influence behavior when preferences are aligned (Crawford and
Sobel 1982).4 The intuition is fairly simple. Players whose preferences are similar have strong incentives to provide high quality information to each other in order to reach the outcome they both desire. Farrell and Rabin nicely articulate the intuition of this result:
“A misinformed listener will do something that is not optimal for himself and, if their interests are sufficiently aligned, this is bad for the speaker too. In a nutshell, this is how cheap talk can be informative in games, even if players ruthlessly lie when it suits them”
(Farrell and Rabin 1996, pg. 104).
Farrell and Gibbons identify a second bargaining environment in which cheap talk may be rational. Cheap talk can be effective if parties have the ability to communicate with each other before formal negotiations commence. By signaling a willingness to negotiate, players can change each other’s beliefs about the prospects for a bargain, creating second-stage bidding strategies that would not otherwise have existed in equilibrium. This two-stage process makes participation endogenous, (i.e., it allows actors to choose whether to negotiate after the cheap talk stage), and enables the actors to trade off “bargaining position against the probability of continued negotiation” (1989, pg.
229).5
Sobel offers a third model. Cheap talk can also affect bargaining outcomes when there is repeated interaction and uncertainty about a sender’s interests. If a receiver is unsure about whether a sender’s interests are similar, cheap talk can be used effectively, in early periods (Sobel 1985). Sobel reveals that in equilibrium an unfriendly sender can
4 Babbling equilibrium, where signals are random and do not convey information, can still exist even with perfectly aligned preferences (Crawford 1998, pg. 288). 5 Other models of bargaining also show how cheap talk can have an effect on bargaining in equilibrium (Matthews 1989). exploit a receiver by transmitting information truthfully in early periods of interaction only to deceive the receiver later on. According to Sobel, “[i]f an agent is uncertain about the motives of someone…then the extent to which he trusts the other will be based on the partner's earlier actions. Thus there is an incentive for an enemy to behave like a friend in order to increase his future opportunities, and for partnerships to last until someone cashes in.”6
Crawford has modeled how lying can be advantageous against actors who are not fully rational (Crawford 2003). Crawford starts by making an important assumption.
What if some individuals have different beliefs about the world and costless communication can be used strategically to exploit these beliefs? Crawford shows that less “sophisticated” players (called mortals) can be influenced by cheap talk in ways that truly rational players can not.7
Economists, however, are not the only ones who have attempted to understand the puzzle of cheap talk. In a book about diplomacy, Anne Sartori has shown that states can benefit from this type of communication despite its costlessness (Sartori 2005). She argues that states that develop a reputation for bluffing are less successful in using diplomacy to achieve their goals than states that communicate sincerely.
Each of these models reveals that cheap talk is not meaningless. Under certain conditions even the cheapest communication can play a critical role in changing equilibrium behavior. What we are less sure of is when and how this type of talk is actually used.
6 Sobel p. 570. 7 Crawford, p. 137. Experimental Analysis of Cheap Talk
A few experiments have been conducted to analyze the role of cheap talk in different settings, and the results are mixed. Early research focused on the role of cheap talk in coordination games, or in coordination games with mixed motives (like the “battle of the sexes”). Communication was either structured (there were restrictions on the sequencing or content of messages) or it was unstructured and was used to signal intentions. Whether cheap talk had an effect depended on the interaction between the type of communication and the underlying strategic context (Crawford 1998, pg. 294).
For example, coordination was much more likely to occur in a battle of the sexes game with one sided communication than with two sided communication (Cooper, DeJong et al. 1989). On the other hand, cooperation was more likely to occur in “stage-hunt” situations under two sided communication rather than one-sided (Cooper, DeJong et al.
1994).8
Several studies have looked at the role of cheap talk in public goods provision experiments. Isaac and Walker and others have found that face to face communication between subjects can increase the contributions they make (Isaac and Walker 1988;
Ostrom, Gardner et al. 1994). Palfrey and Rosenthal study a public goods game with incomplete information about private endowments (Palfrey and Rosenthal 1991). They find that while subjects regularly conditioned behavior on the cheap talk message they received, they did not obtain more efficient outcomes as a result. Wilson and Sell investigate the interaction between pre-play communication and reputation (Wilson and
8 In the battle of the sexes one sided communication is used to break the symmetry (payoffs to one player are the transpose of the other player’s payoffs) of the underlying game, whereas the stag-hunt game does not require this symmetry to be broken in order to obtain the efficient outcome. Sell 1997). They find that when both pre-play communication and information about past behavior are available, subjects contribute more than when only one of these information sources is present. They also find, surprisingly, that subjects contribute the most when they cannot communicate at all and have no information about past behavior.
An important difference between their experiment and those of Isaac and colleagues is that communication was done anonymously and through the computer instead of in a face-to-face setting.
Finally, Forsythe and colleagues investigated a bargaining game with incomplete information about the division of a pie (Forsythe, Kennan et al. 1991). They found that individuals did not behave much differently if they were allowed to use cheap talk versus if they were not. Croson and colleagues, however, found that in an ultimatum game with incomplete information about outside options cheap talk could affect behavior temporarily.9 Subjects could increase their short term bargaining outcomes by using cheap talk, but could be punished in the long term if they had lied (Croson, Boles et al.
2003). In a series of experiments regarding the way in which cheap talk could be communicated (e.g., face to face versus written statements), Valley and colleagues found that cheap talk did help subjects reach bargains (Valley, Moag et al. 1998). Finally, in an experiment most closely related to our own, Sundali and Seale (2004) found that in an n- person market entry game where entrants were allowed to issue costless signals, subjects exaggerated their intention to enter. Cheap talk, however, had little impact on the behavior of others and thus did not increase market coordination.10
9 This was the case if it was possible to detect lying. 10 Our interest is most directly in line with that of Croson and colleagues in that we are interested in the role of cheap talk in bargaining environments. Our investigation differs from theirs in several important ways. They looked at the role of reputation within a pair of actors who repeatedly interacted with each other. Our study looks at behavior where a single “defender” These mixed results indicate that more work need to be done to tease out behavior. In particular we believe that the role of cheap talk should be investigated in other well-known strategic settings. We hope this study contributes to a better understanding of the set of contexts where cheap talk does or does not influence behavior.
Cheap Talk and Reputation Building
In what follows, we look to see if cheap talk affects behavior in an entry- deterrence game with incomplete information about the defender’s type. We choose an entry-deterrence game for three reasons. First, the game has the sequential structure that allows us to observe when defenders are likely to issue threats, and how different entrants in different periods react to these threats. Second, we know from individual case studies in international relations that governments have used verbal threats in an attempt to deter potential attackers. (Give examples) The challenge in the laboratory is to reveal the conditions under which these threats are likely to be used, and what effect, if any, they have.
We restrict our experiment to threats that are not expressed publicly. We do this because it allows us to observe threats in their most costless form. Since threats cannot be observed by other players, there are no incentives for the sender to follow through with threats for reputational reasons (e.g., in the ways in which Sartori models and
Wilson and Sell investigate). This is especially true since defenders know that they will interact with each entrant only once. Thus, senders gain no additional deterrent value by
faces a series of different challengers. In experimental speak, we use a “strangers” design whereas theirs uses a “partners” design. The strategic game we study also differs. They use a repeated ultimatum game with outside options, whereas we use a repeated entry-deterrence model. publicly validating their threats. Recipients should also be far less likely to be deterred by threats issued privately than those that are not. Thus, the structure of our experiment is a particularly hard test for the influence of cheap talk on behavior.
The Structure of the Game
Figure 1 shows the structure of a single-shot play of the “entry-deterrence game” as well as payoffs for the entrant and defender. In this game, an existing monopolist can dissuade smaller firms from entering a lucrative market by engaging in predatory pricing.
By paying the short term costs of a price war, the monopolist can signal to other firms that it is likely to do so again in the future. Thus, the short term losses from predatory behavior are offset by long term gains from deterrence.
An important element of the game is that there is incomplete information about how tough the defender is likely to be when challenged. Entrants don’t know if defenders are committed – willing to fight to deter entry under all conditions – or if they are uncommitted and not willing to fight unconditionally. This creates an opportunity for cheap talk to be used. Theoretical Predictions Without Cheap Talk
The standard way to solve the repeated chain store game with multiple entrants is to identify a sequential equilibrium. Details of this derivation are in (Jung, Kagel et al.
1994) and the classic statements are in (Kreps and Wilson 1982; Milgrom and Roberts
1982). Strong type defenders should always fight no matter what period they are in.
Weak type defenders, on the other hand, play a more mixed strategy. In early periods, weak defenders should always fight in order to help deter entry in future periods.
However, upon reaching a certain point in the game, weak defenders should fight with decreasing probability. That’s because there are fewer benefits from maintaining a reputation for being a strong so that by the last round, weak types never fight.
The behavior of entrants depends on how the defender behaved in earlier rounds.
If a defender backed down in an earlier period, then the entrant should always enter. If the defender never backed down, entrants should pursue a fairly specific strategy.
Entrants should never enter in the early periods, as they will either be met by strong types or weak types that always fight in equilibrium. During the middle and latter periods they should enter with a higher probability, and should continue to enter at this probability for the rest of the game. Table 1 graphs these probabilities of entry or fight for the case where there has been no previous backing down.
Theoretical Predictions With Cheap Talk
We do not directly model how cheap talk is likely to affect behavior, but we do offer three basic predictions based on the conventional wisdom.11
11 While a formal model would ultimately be an important step given the prominent role of the game we study (as popularized by the “Gang of Four” in the early 1980’s), our goal is investigate the role of cheap talk empirically. Several of the experiments we reviewed offered reasons why H1: Defenders should be indifferent between issuing a threat and not issuing a threat.
H2: Defenders who threaten to fight should be no more likely to fight than those who did not.
H3: Defenders who issue a threat will not deter any more entrants than those who do not.
Experimental Design Without Communication
Subjects were assigned randomly to two separate groups - entrants and defendants
- which were referred to simply as first movers and second movers. These neutral terms were used in order to avoid leading the subjects in any way. Second movers (defenders) were also assigned a ‘type,’ either weak or strong, which we called ‘type 1’ or ‘type 2’.
Strong types prefer fighting after entry whereas weak types do not. This information was not shared with first movers (entrants), who were only told that each defender in the room had a 1/3rd chance of being a strong type.
Both the defenders and the entrants knew how many entrants a defender would face in a single repetition of the experiment.12 Entrants were also given information on how a defender played against all other entrants.13 If a previous entrant had chosen to challenge the defender, all subsequent entrants would see whether the defender had backed down or stayed tough. The history of play allowed entrants to update their beliefs about what type of defender they were likely facing.14
cheap talk should or should not matter, but also do not formally substantiate these claims (e.g., (Wilson and Sell 1997)). We see this as an opportunity for future research. 12 Note that each entrant played each defender once within a ‘repetition’ of the experiment. 13 Note that if an entrant chose not to enter, then the defender’s decision would not be recorded and transmitted to the remaining challengers. 14 Subjects were informed of their identity (first mover or second mover) at the beginning of the experiment but the second mover ‘type’ could change from one ‘repetition’ of the experiment to another. The experiment proceeded as follows. Entrants faced the defenders sequentially.
Entrants were asked to choose between A1 and A2 (entry and not entry). Defendants were asked to select a strategy based on what an entrant might do: ‘if the first mover enters I will choose B1 or B2’ (fight or not fight).15 Each entrant made one decision with no available history (in the first period), one decision with a previous period’s history against a different defender (in the second period), and so on. This design allowed us to keep all subjects engaged throughout the experiment, as well as maximize the amount of data we could collect within an experimental session. After each entrant had played each defender once, subjects saw a screen with their decision history, the decisions of the subject they were paired with in each period, and their own payoffs.16 Subjects were allowed to write these payoffs down to compare with future repetitions of the experiment.
Subjects knew that these payoffs, expressed in points, would be translated into US dollars at the end of the experiment.
Each repetition was repeated five times in order to take into account the effects of learning and to generate sufficient data for the analysis. The precise number of repetitions was unknown to subjects, and they were simply told that the experiment “may or may not be repeated” in order to limit attempts to build reputations across repetitions.
The sequence of entrants a defender faced, and the sequence of defenders an entrant faced, were randomly generated across repetitions and all matching was entirely anonymous with subjects seated at separate partitioned computer terminals. 15 This is known as the strategy solicitation method and is commonly used by experimentalists. We did this to observe the decision of a defender even when their opponent did not choose to enter. While in principle the mechanism of strategy solicitation can influence choices, we note that behavior in our no communication treatment is very similar to that observed by (Bolton and Ockenfels 2007) whom elicited strategies sequentially. Furthermore, we compare two treatments that used the same protocol. 16 Payoffs to other players were not revealed in order to isolate the effect of learning across instead of within repetitions of the 8 period experimental round. Experimental Design With Communication
After completing the first treatment, subjects were told that we were making a slight change in the experiment. This meant that our cheap talk experiment was run on a set of subjects with experience in the strategic environment of the repeated entry- deterrence game, with all subjects keeping either their entrant or defender roles. We explained that defenders would now be able to communicate to entrants whether they would fight or not. Defenders could do this by sending the following message through the computer: “if you choose enter, I will [fight, not fight].17 This message was seen only by the immediate entrant and not by later challengers, mirroring private communication that occurs between leaders engaged in closed door negotiations.
Everything else in the experiment was the same as our baseline design.18
Subjects were recruited through Princeton University’s Laboratory for
Experimental Social Science (PLESS) using an e-mail solicitation to all Princeton students who had signed up with the lab.19 Those who responded were accepted until all positions were filled. Students entered the laboratory one by one and were seated at computer workstations that were separated by pull out dividers to prevent interaction
17 Our experiment used neutral descriptions, and thus subjects actually chose between “I will (not) choose B1 if you choose A1. We did not allow subjects to not send a message. 18 It is important to note several aspects of our communication design vis a vis some of the principles discussed earlier in the paper. First, communication was anonymous and subjects were not able to isolate the identity of the person from whom they received a message. Second, communication was structured in a one way setting and with a constrained message space. Only defenders were able to send a communication. Finally, communication was private, and thus subsequent entrants were unable to triangulate communication and behavior. We made these decisions for several reasons. Communication was kept anonymous because everything else in the experiment was kept anonymous. Communication made available in a constrained message space in order to simplify analysis and focus on the role of threats and the willingness of defenders to send these threats. Communication was one way because we investigated a game of one-sided incomplete information. 19 Each separate experiment session drew subjects from the same population, although subjects that had participated in our experiment previously were not allowed to participate again. between subjects. Instructions were then read to all participants. During this process subjects were given the opportunity to make practice decisions and review a set of questions and answers about the experiment. Any questions from subjects were repeated and answered so that all subjects could hear. This ensured that all aspects of the experiment design were common-knowledge.20 Subjects were paid one by one at the end of the experiment with money earned in the experiment and a guaranteed $10 ‘show-up’ fee. The experiment was programmed and conducted with the software z-Tree
(Fischbacher 1999).21 In each experimental session there were 16 subjects, 8 defenders and 8 entrants.22
Results and Interpretation
In this article, we were interested in testing three basic predictions. First, would all defenders engage in cheap talk if given the chance (H1)? Second, would defenders who issued a cheap talk threat be more likely to fight (H2)? And third, would entrants be less likely to challenge if a threat had been communicated (H3)? The results, which we discuss below, are quite surprising.
Our empirical strategy for all of our hypotheses is to break defenders out by those who had already backed down and those that had not. We also break out entrants into those that face a defender who had not yet backed down, and those that faced a defender who had. We do this because the equilibrium model we discuss above makes this
20 The instructional materials are available from the authors. 21 Our design, instructions, and computer interface went through a lengthy piloting period in order to obtain the best possible experimental protocol. 22 We implemented the second treatment—allowing for cheap talk—in two of our sessions. Other experimental sessions only implemented the first treatment. Including these other sessions in our analysis does not change our conclusions, but in order to draw the clearest comparisons we only include in this analysis the sessions where we ran both treatments. A separate paper gives a complete analysis of all the no-communication treatment sessions (Tingley and Walter 2007). important distinction, and we do not want to conflate reputational effects with the effect of cheap talk. Next, we calculate either the mean rate of a behavior (e.g., taking the average of cases where entry=1 and no entry=0) and calculating test statistics using standard difference in means tests or we calculate proportions and calculate test statistics using a proportions distribution. These statistics produce largely identical inferences but given our sample sizes and the sampling distribution of these statistical tests there can be slight differences.23 We report both to be statistically transparent.24
Hypothesis 1: Defenders should be indifferent between issuing a threat and not issuing a threat.
Contrary to expectations, we found that defenders were not indifferent to making a threat or not making one. In fact, almost all defenders chose to issue a threat when given the opportunity. As Table 2 shows, weak defenders engaged in cheap talk nearly
89% of the time, whereas strong defenders did so 95% of the time. Table 3 shows that the number of threats stayed relatively constant throughout the 8 periods. The fact that defenders had a strong preference for making verbal threats suggests that defenders believe that threats are likely to have some positive effect (or at least not a negative effect) in deterring a challenge even though they could not be punished for not following through.