We experimentally study optional costly communication in Stag-Hunt games. Prior research demonstrates that efficient coordination is difficult without a communication option but obtains regularly with mandatory costless pre-play messages. We find that even small communication costs dramatically reduce message use when communication is optional, but efficient coordination can occur with similar frequency as under costless communication. These findings can be accounted for by formalizations of forward induction that take Nash equilibrium as a reference point (such as Kohlberg and Mertens in Econometrica 54: 1003–1037, 1986; Govindan and Wilson in Econometrica 77: 1–28, 2009), while formalizations that only appeal to (higher-order) knowledge of rationality remain silent in this environment.
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Weak-Link games have been experimentally studied by, for example, Van Huyck et al. (1990), Weber et al. (2001), Weber (2006) and Brandts and Cooper (2006) and represent useful models of varied economic activity, such as investment or production under complementarities (Bryant 1983; Hirschleifer 1983; Knez and Camerer 1994).
For theoretical analyses of the effectiveness of unilateral vs. multilateral communication, see Ellingsen and Östling (2010). In experiments, Cooper et al. (1992a, b) find that two-sided communication is more efficiency enhancing than one-sided communication. Weber et al. (2001) and Chaudhuri et al. (2009) find varying effectiveness of limited forms of communication. Other experimental evidence provides instances in which one-way communication yields high levels of efficiency (Charness 2000; Duffy and Feltovich 2002; Brandts and Cooper 2007) or even out-performs two-way communication (Burton et al. 2005). Related research studies the effects on coordination of communication through different kinds of institutions (Kogan et al. 2011; Shurchkov 2016).
A few recent studies explore costly pre-play communication in coordination games. Manzini et al. (2009) consider pre-play communication unrelated to game strategies—i.e., “smiles” that players can send to one another prior to playing the game. The use of smiles, though infrequent, slightly increases the frequency with which players select more efficient actions, but this infrequent use is insufficient to yield better coordination. When smiles are costly, they are used very infrequently (in less than 1 % of cases). Fehr (2011) finds that players rarely vote to impose a costly communication regime, prior to merging two three-person groups playing a coordination game, resulting in coordination failure. This suggests that people fail to properly anticipate the benefit of costly pre-play messages in large groups. A similar finding is observed by Kriss et al. (2016), who study optional costly communication in Weak-Link games. Andersson and Holm (2013) study two-sided costly communication in a market-entry coordination game. While sending messages aids coordination, subjects attempt to free-ride by refraining from sending messages in the hope that other players will do so.
In the online appendix we analyze the forward induction implications of Pearce’s (1984) extensive-form rationalizability, shown by Battigalli and Siniscalchi (2002) to correspond to rationality and common strong belief in rationality on complete type spaces; iterative admissibility, where in each round all weakly dominated strategies of all players are deleted (Brandenburger et al. (2008) demonstrate that m + 1 rounds of iterative deletion of weakly dominated strategies corresponds to rationality and m-th order assumption of rationality with complete type structures); and fully permissible sets, which where proposed by Asheim and Dufwenberg (2003). We show that none of these solutions concepts has explanatory power in the Stag-Hunt game with optional costly communication and reasonably costly messages.
The analysis is available from the authors upon request.
Alternatively, our forward-induction prediction can be obtained by applying Kohlberg and Mertens’ (1986) “never weak best reply” criterion, which requires that solutions be stable against the elimination of strategies that are not a best reply against any equilibrium supporting the solution.
Our game has mixed strategy equilibrium outcomes in which all message options, sending no message, sending message 1 and sending message 2, have strictly positive probability. While these outcomes pass the Govindan–Wilson test, persistence and the minimal curb condition suggest that these outcomes are fragile.
Other than the treatment differences, our design choices generally follow those of Cooper et al. with the exception that we simplified procedures where possible and modified the design to collect more data. For example, instead of using 11 subjects with one excluded each period, we used 10 subjects. Instead of 11 practice rounds of a dominant strategy game followed by 22 real rounds, we included no practice rounds and 40 real rounds. Instead of each subject being matched with every other subject exactly twice, we used random matching. And finally, instead of a payoff procedure that involved a lottery, we directly converted all experimental earnings into U.S. dollars.
The experiment was programmed and conducted with the software z-Tree (Fischbacher 2007). Instructions for one treatment (with \( c = 10 \)) are provided in the online appendix.
As expected, message “1” was sent very rarely (never more than 1.2 % of the time in any condition). In a large majority of these cases (86 %), subjects followed a message of “1” by playing action 1, and no subject sent message “1” and subsequently chose action 2 more than one time in the forty periods.
Throughout our analysis, we report linear models to facilitate interpretation of the coefficients. Appendix C (available online) presents probit models that better account for the binary dependent variable and produce similar results. We also estimated the models in Table 3 that include more than one period of data with period fixed effects; the results are substantively unchanged.
In a more conservative statistical test, we calculate the frequency of message “2” use in a session and use this session-level statistic as the unit of observation in a non-parametric Wilcoxon rank-sum test of differences across conditions. The difference in frequency of message “2” use between the Costless Message condition and either RC-10, RC-100, or UC-300 is statistically significant (respectively, z = 2.39, p < 0.02; z = 2.39, p < 0.02; and z = 2.24, p < 0.03). Among the conditions with Costly Messages, only the difference between RC-10 and UC-300 is statistically significant (z = 2.36, p < 0.02).
The coefficients for the three Costly Message conditions in model 1 differ significantly and are ordered such that fewer messages are used as costs increase. While our predictions do not account for any differences between the three treatments with costly messages, it is not entirely surprising to find fewer messages with higher costs.
Three subjects in Costless Messages rarely or never sent message “2” even though doing so was costless. One of these subjects informed us, at the end of the experiment, that he had poor vision and experienced difficulty reading the screen and clicking on the radio buttons. The other two repeatedly played action 1, and sent the corresponding message, perhaps out of altruism (i.e., to ensure that their opponents did not receive the zero payoff).
Note that there is a slight gap that opens up between UC-300 and No Messages in the second half of the experiment (as we show below in Table 4, the time trend differs significantly for these conditions). This is due to heterogeneity across sessions in the No Messages condition (see Fig. 5 and Appendix Figure C.1 online). In two sessions, convergence to action 1 occurred as predicted, while in the remaining No Message session behavior converged to action 2. Therefore, coordination on the inefficient subgame equilibrium (1,1) is weaker than that observed by Cooper et al. (1992a, b), though we find it to be the case in two of three sessions. Some procedural differences between the two experiments may explain the disparity (see footnote 11).
As with Table 3, we re-estimated the relevant models with period fixed effects and find no substantive change. Also as with Table 3, we studied whether experience with opponents’ prior message use affects action choices. Specifically, we estimated a version of model 1 in Table 4 that includes an additional explanatory variable identifying whether a subject’s opponent in the prior period sent a message. The coefficient for this variable is statistically insignificant and its inclusion has no substantive effect on the other variable coefficients.
Note that the Costless Messages data in the (none, 2) panel is almost entirely composed of the three subjects with irregular message behavior (see footnote 16). The Costless Messages data in the (2, none) panel is composed almost entirely of responses to these subjects by their opponents.
The frequency of action choice 2 under Costless Messages in the top-left (none, none) panel is not highly informative as this message profile occurred very infrequently.
The negative coefficients on the interaction between the costly message conditions and Message “2” indicate that the effect of receiving a message is weaker under costly messages than under costless messages.
This occurred 40 % of the time in RC-10, 63 % in RC-100, 92 % in UC-300, and (by construction) 100 % of the time under No Messages. The no-messages case did not occur under Costless Messages, where every pair in Period 1 had at least one message, so we omit this condition from the model.
We find some evidence that subjects in RC10 and RC100 learn to play action 2 in response to not observing a message from an opponent. Specifically, if we consider cases in which (1) a subject played action 1 in period t − 1, (2) the subject’s opponent in period t − 1 sent no message, and (3) neither the subject nor the current opponent sent messages in period t, then subjects whose period t − 1 opponent played action 2 are more likely to play action 2 (25 % of the time) than those whose period t − 1 opponent played action 1 (5 %). This difference in proportions, which is highly significant (z = 7.99, p < 0.001), suggests that at least some subjects learn through experience to have confidence that an opponent will play 2 even in the absence of messages.
To account for possible noise in the data, our hypotheses stated predictions in terms of modal behavior. More precise predictions correspond to the corner in each quadrant where message and action frequencies are either 0 or 1.
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We are grateful to the Pittsburgh Experimental Economics Laboratory (PEEL) for access to laboratory resources, to the National Science Foundation (Award SES-1021659) for partially funding this research. Blume’s stay at the Institute for Advanced Study was funded through a Roger W. Ferguson, Jr. and Annette L. Nazareth Membership. We appreciate helpful comments from participants at several seminars and conferences. We are especially thankful to Björn Bartling, Marco Battaglini, Pierpaolo Battigalli, Emiliano Catonini, Alain Cohn, David Cooper, Donja Darai, Ernst Fehr, Drew Fudenberg, Holger Herz, Steven Leider, Robert Östling, Frederic Schneider, Joel Sobel, Alistair Wilson, and Robert Wilson for thoughtful feedback on earlier drafts.
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Blume, A., Kriss, P.H. & Weber, R.A. Pre-play communication with forgone costly messages: experimental evidence on forward induction. Exp Econ 20, 368–395 (2017). https://doi.org/10.1007/s10683-016-9487-y
- Forward induction
- Stag hunt