Experience in public goods experiments

We acknowledge that we use the term “history” with a meaning different from the one common in the public goods literature. History is generally used to signify the decisions that a player observes during the game (e.g., Gunnthorsdottir et al. 2007).

A different fundamental methodological issue, which focuses on the misrepresentation of social preferences in laboratory experiments with student samples, is addressed by Falk et al. (2013).

We chose this protocol to minimize strategic effects of repeated play and to allow for revisions to beliefs only at the population level.

To simplify notation, we always refer to player i’s partner as j, although this is a different person in each period.

In our experiment, we elicited beliefs about the others’ contribution. The previous research in experimental economics has shown that the mere act of eliciting beliefs can affect behavior in finitely repeated public goods games (see, e.g., Croson 2000 or Gächter and Renner 2010), although the evidence regarding the undesirable effects of belief elicitation procedures is far from being conclusive (e.g., Wilcox and Feltovich 2000) and does not concern stranger matching protocols.

See Selten (1998) for an axiomatic characterization of the rule, and Offerman et al. (2009) for an experiment investigating its behavioral properties.

A similar rule has been used, e.g., by Offerman et al. 1996, Costa-Gomes and Weizsäcker 2008, and Rey-Biel 2009, although there exists no consensus among experimentalists about the optimal incentive mechanism for eliciting beliefs. Huck and Weizsäcker (2002) compare beliefs elicited via a quadratic scoring rule with beliefs elicited via a Becker–DeGroot–Marshak pricing rule, and find that the former yields more accurate beliefs.

In the instructions, we use a verbal description of the rule and give numerical examples. Recognized problems of the quadratic scoring rule are that incentives are flat at the maximum and that this may be difficult to understand. To avoid the latter problem, our instructions emphasize that the more accurate the beliefs, the higher the payment.

From the experimental instructions, it can be noted that the explanation of the public good in our experiment is different from that used in other studies (e.g., Fischbacher et al. 2001). Yet, we are confident that participants understood correctly the social dilemma feature of the framework which they were confronted with. We base our statement on the following facts: (1) instructions were read aloud in each session to establish public knowledge of the fact that all participants in the session were facing the same experimental instructions and nothing was concealed; (2) participants had to solve some control questions (reported in the Online Appendix F) before starting the experiment; (3) contribution data and belief data from our experiment do not present any anomaly that might induce an analyst acquainted with the literature on public goods experiments to believe that something went out of control.

The first six sessions of treatment I have already been analyzed in Conte and Levati (2014).

We acknowledge that a stricter baseline would have had completely inexperienced subjects. However, since other researchers were using the laboratory at the time of our data collection, the recruitment of completely inexperienced subjects would have implied stopping all the ongoing experiments. In our econometric analysis, we control for the time passed from the first and/or last participation in an experiment, and therefore, we are able to distinguish between subjects who were participating for the first time and subjects who had already participated in experiments. These factors are found not to improve the econometric specifications.

Note that, on the basis of the information provided by the ORSEE system, we are only able to observe whether a subject has taken part in an experiment or not. We cannot observe other characteristics of the experiment, as, for example, matching protocol, money earned, length and repetitiveness of the interactions, etc.

By “expected contribution”, we mean the amount that subject i expects his partner j to contribute in each period t. These amounts are calculated by averaging all possible contributions, weighted for the corresponding beliefs. More exactly, expected contributions in period \(t=1,\ldots ,15\) are computed as

Given our rematching protocol, the number of statistically independent observations is 7 in both treatments.

To assess the accuracy of beliefs, along the lines of Eq. 2, for each individual i in the two samples, we derive the following index:It represents the square root of a quadratic deviation of subject i’s beliefs from the empirical distribution of contributions: the lower \(\delta _{i,t}\) is, the closer the subject’s beliefs are to such a distribution.

We thank an anonymous referee who noted how it may seem surprising that, in the first periods of play, beliefs are less accurate (or better, similarly accurate) for the experienced than for the inexperienced. This may be due to the fact that the experienced do not know that they are interacting with other experienced subjects, so they may reasonably assume that their opponents are drawn from the general population composed of participants with different degrees of experience. As the experiment proceeds, however, the experienced subjects adjust their beliefs faster compared to the inexperienced ones.

To estimate the model, we divided contributions by 10.

Details can be found in Train (2003).

Identification fails in the following cases: when, given i’s distribution of beliefs and Eq. (9), i’s optimal contribution is always \(c_{i,t}=0\) (in that case, a conditional cooperator is indistinguishable from a selfish agent); when, given i’s distribution of beliefs and Eq. (9), i’s optimal contribution always corresponds to the median of i’s observed contributions, \(c_{i,t}=m_{i}\), (in that case, a conditional cooperator is indistinguishable from an unconditional cooperator); when subjects’ preferences are not stable throughout the game. In those cases, individual’s type identification is achievable (or refined) via repeated observations.

All the tests reported here are bootstrapped (200 replications) with asymptotic refinement (see Cameron and Trivedi 2005, among others).

The estimated relative proportion of selfish subjects with respect to conditional cooperators is 0.195 (s.e. 0.041) and 0.328 (s.e. 0.062) from sample I and E, respectively, the latter being significantly different from the former (\(z=2.12\), p-value \(=0.03\), two-sided test). However, this result does not exclude a different redistribution of types due to experience (for example, with conditional cooperators learning how to play the dominant strategy and unconditional cooperators conditioning their choices on beliefs).

The numbers in Table 4 have to be interpreted as follows. Specification 1 attests, for example, that, if we draw two samples which are equal in everything but in subjects’ experience, then we have to expect to find in the experienced sample, with respect to the inexperienced sample, that the proportion of selfish (conditional cooperator) is 6.37 (6.81) percentage points larger and the proportion of unconditional cooperators is 13.18 percentage points smaller.

Table 4 only reports the relevant results. We used several different controls such as the number of participations in a particular type of experiment, the time passed from the first and/or last participation in an experiment both for social dilemma and other experiments, course of study, and so on. None of them seem to improve upon the specifications displayed in the table, but are available from the authors on request.