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Public disclosure of players’ conduct and common resources harvesting: experimental evidence from a Nairobi slum

Abstract

We evaluate the effect of information disclosure (feedback on individual contributions and payoffs) on players’ behavior in a multi-period common pool resource game experiment run in an area of notably scarce social capital, such as the Nairobi slum of Kibera. We document that cooperation significantly declines over rounds when such information is revealed. Our results are consistent with the Ostrom (J Econ Perspect 14:137–158, 2000) hypothesis that, in the absence of formal punishment rules, the availability of information about individual behavior makes common resource management more difficult and tragedy of the commons easier.

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Fig. 1

Notes

  1. 1.

    The concept of social capital presents a multidimensional character (e.g., Paldam 2000). Many definitions of the concept have been proposed and two main approaches may be identified in the literature. On the one hand, social capital is defined in terms of social norms of trust and reciprocity that fosters cooperation (e.g., Putnam et al. 1993; Knack and Keefer 1997). On the other hand, social capital is intended in terms of cooperative networks of relationships among agents (e.g., Coleman 1988; Lin 2001; Burt 2002). For the purpose of this contribution, that is, to analyze the effect of information disclosure without formal punishment rules on cooperation in a CPRG, we mainly refer to the first approach.

  2. 2.

    Cassar and Wydick (2010) show that the average players’ contribution rate in a group lending experiment is dramatically lower in the Kibera slum than in other poor areas in Armenia, Philippines, India, and Guatemala. Greig and Bohnet (2008) show in a one shot investment game experiment that Nairobi slum dwellers adhere to a balanced reciprocity norm (quid-pro-quo returns for any level of trust according to which second movers return a fixed amount whatever the amount sent), which generates lower cooperation with respect to the conditional reciprocity norm (a positive relation between the amount sent and the fraction returned) prevalent in developed countries.

  3. 3.

    In this respect, our approach closely follows Henrich and Smith (2004) and can be related to the recent literature on the effects of feedback schemes on voluntary contribution mechanisms. In such literature, these schemes are regarded as frames that affect players’ beliefs, which in turn affect their actions. Nikiforakis (2010) shows that feedback on contributions leads to more cooperative attitudes than feedback on payoffs. This presumably happens because the first format leads participants to focus on cooperation opportunities, while the second on private benefits. Bigoni and Suetens (2010) allow participants to choose among the two feedback mechanisms and show that high contributors prefer to know about contributions, while low contributors about payoffs. Our experimental setting differs in a few elements with respect to this literature. As in Henrich and Smith (2004), who also perform their experiment in low income socioeconomic environments, we provide information on both contributions and payoffs (in this order) and are the first to our knowledge to run such experiment in a Nairobi slum. In particular, with our design, we aim to study in this particular socioeconomic environment the effect of monitoring without well-defined sanction rules on common resources harvesting.

  4. 4.

    Without members’ reshuffle across rounds one might expect reputation effects to be stronger and the propensity to free ride lower when monitoring is allowed, also because we may expect a self-enforcement mechanism due to relationships outside of experiments inducing more cooperation in the PIT than in the RIC. This makes our findings more counterintuitive. Consider, however, the fact that our results on the monitoring effect on players’ behavior are not in contrast with the evidence collected by Cassar and Wydick (2010) in a group lending experiment. The authors find that when group members are informed about the others’ decision to contribute or not to the repayment of the loan, the negative effect of retaliation against defectors may exceed the positive shame effect associated with the peer monitoring. The authors conclude that “peer monitoring seems to outperform no peer monitoring only until any type of malfeasance emerges within a borrowing group. When malfeasance does begin to occur, cooperation unravels more quickly under peer monitoring” (Cassar and Wydick 2010, p. 736). Moreover, consider that a self-enforcement mechanism based on sanctions connected with relationships outside the experiment may emerge if social interactions are stable and capable of making sanctions effective. This seems not to be the case in the context where we ran the experiment (see footnote 2). Finally, notice that the reduced heterogeneity in group composition across rounds induced by lack of reshuffle will be controlled for with (i) checks of balancing property between treatment (PIT) and control (RIC), and (ii) fixed effects estimation (see Sect. 4).

  5. 5.

    We would like to thank an anonymous referee for this suggestion.

  6. 6.

    The author considers the following variables as affecting the probability of users’ self-organization (Ostrom 2009): Size of resource system, Productivity of system, Predictability of system dynamics, Resource unit mobility, Collective-choice rules, Number of users, Leadership/entrepreneurship, Norms/social capital, Knowledge of Social-Ecological System/mental models, Importance of resource.

  7. 7.

    In this respect, the Harambee—a traditional custom in Kenya (Waithima 2012) that involves a vast majority of residents (around the 90 % of residents according to the survey by Barkan and Holmquist 1986) and also widespread in the area in which we ran our research (Greig and Bohnet 2009)—shares many characteristics of our design. Harambee means “let’s pull together” (Miguel and Gugerty 2005). It denominates the bottom-up collective effort in providing goods, usually social infrastructures (Wilson 1992) through the voluntary cooperation of members and often implies public meetings (i.e., face-to-face interactions) to collect contributions to the good. However, while the common pool resource game, where the initial common endowment may be interpreted as the common resource, is better suited to study the “tragedy of commons” exploitation problem, the harambee phenomenon could have been better mimicked through a standard public good game, where subjects have to decide how much contribute to the good, as it is for this kind of practice. This is also because in the harambee participants have to put some of their own resources in the “pot” to finance local public goods, while in our game the pot with the money is already there and players may withdraw from the pot money which is not taken originally from their pockets.

  8. 8.

    We refer to formal sanctions at the community level since the individual decision to withdraw more in a later round may be considered a form of informal punishment at the individual level and is an option available among players’ strategies in our game.

  9. 9.

    Half of all households in Nairobi slums are classified as “food insecure with both adult and child hunger” and 70 % of inhabitants live below the poverty rate. The cost of basic needs in Nairobi was calculated to amount to 100 Kenyan shillings per day per member in 2007 (Faye et al. 2011).

  10. 10.

    The inclusion of the CPRG experiment into the “TG-sandwich” experiment we described above implies that we have to control for what happens in the first TG round. We do it in our fixed effect estimation (see Sect. 4).

  11. 11.

    Notice that the average contribution decreases only slightly and non-monotonically after the first round. This is not at odds with a recent contribution according to which “the meta-analysis did not find that the number of periods in a session had a significant effect. However, a separate analysis showed that at least in those studies where data were reported, contributions declined sharply between the first and last periods. This suggests that there may be a non-linear relationship between repetition and contributions, probably at least partly because of end-gamepg effects.” (Zelmer 2003, p. 305). Since players involved in our game do not know the exact number of rounds they are going to play, we may assume the end-game effect at least partly reduced in our setting, thus justifying our evidence on relatively stable average contributions over time.

  12. 12.

    Ideally, to net conformity out of conditional cooperation effects we should be able to isolate pure imitation arguments (i.e. not necessarily based on payoff maximization) from payoff-based strategies. This would have been possible in presence of information on players’ behavior outside one’s own group.

  13. 13.

    Our results do not significantly change if we use the withdrawal amount instead of the withdrawal rate. Results are available upon request.

  14. 14.

    By collecting experimental measures of betrayal aversion, Bohnet et al. (2008) show that individuals are generally less willing to take risks when the uncertainty is due to another person rather than nature. In order not to further complicate the game and expose participants to an additional experimental activity, we collect survey measures of betrayal aversion by asking questions on negative reciprocity (see the questionnaire in the Appendix). Those measures should be proxy for betrayal aversion as argued by Fehr (2009), “[...] Betrayal aversion means that people dislike non-reciprocated trust [...] People with a strong preference for negative reciprocity (i.e., a preference for punishing non-reciprocal behaviour) are, ceteris paribus, more likely to feel betrayed in case of non-reciprocated trust [...]” (p. 247). In the questionnaire betrayal aversion is calculated by looking at the level of consent to the following two questions: (i) If I suffer a serious wrong, I will take revenge as soon as possible, no matter what the costs; (ii) If someone offends me, I will also offend him/her.

  15. 15.

    After the game, we ask participants for the number of other participants they can name in order to control for confounding effects deriving from heterogeneous social distance among participants.

  16. 16.

    Note that estimation results obtained with random and fixed effects are confirmed also when we replace the GWR variable with a variable which measures, for each subject \(i\) in group \(j\), the \(j\)-group’s mean withdrawal rate excluding \(i\)’s own withdrawal rate. Results are omitted for reasons of space and are available upon request.

  17. 17.

    These variables allow us to check whether and how player’s behavior is affected by the behavior of the least vs. highest co-operators (i.e., respectively, \({\textit{WITHDRAW\_LESS\_THAN\_MAX}}\) vs. \({\textit{WITHDRAW\_MORE\_THAN\_MIN}}\)).

  18. 18.

    Note that the total number of participants in the experiment included in the estimates drops to 301 since we have three missing data on the TRUSTINDEX variable.

  19. 19.

    Results are omitted for reasons of space and are available upon request.

  20. 20.

    As suggested by Fehr (2009), we also elicit players’ betrayal aversion by asking in a post-experimental survey how much they agree on two statements concerning revenge. On the basis of the answers to these questions we create a dummy variable called “betrayal averse” equal to one if the respondent “strongly agrees” or “agrees” on such statements (see Sect. 10 of the Appendix).

  21. 21.

    This may also occur since each player may infer something about the average withdrawal rate of the group also in the RIC based on information on its withdrawal and on the game payoff. Hence, the PIT may not add much information on that. For instance, if a player withdraws 100 and expects that all the other players in the group will do the same s/he should get (50*4*2)/2 from the pool. If s/he obtains less, it means that other group mates withdrew more than her/him. Note also that—as an anonymous referee suggested—the cooperation decay observed in the RIC (due to the significance of \({\textit{GWR}}_{i,t-\textit{1}}\)) is consistent with the strategies and learning hypotheses by Andreoni (1988) on players’ gradual convergence to the Nash equilibrium because of game repetition. It has to be noted, however, that in our setting players do not know the exact number of rounds they play for and, consequently, the (non-cooperative) dominant strategy does not emerge in the last rounds.

  22. 22.

    Consider two different groups. In the first round, they differ for the average withdrawal rate but they are exactly the same in terms of distribution of players’ choices around the mean. If only the divergence between one’s own decision and others’ decisions affects players’ behavior, we will not observe any difference in the second round between the behavior of players of the two groups.

  23. 23.

    The sign of the coefficient implies that higher than average withdrawal rates in the previous round have positive effects on the following round withdrawal decision.

  24. 24.

    More precisely, the comparison of the magnitude of the general “divergence effect” (ME-GROUP coefficient) with the smaller move toward conformity/conditional cooperation induced by information (ME-GROUP*PIT coefficient) suggests that what we observe is just a reduction of the divergence effect—which is in any case a move toward conformity/conditional cooperation net of the overall sample effect.

  25. 25.

    See the increasing magnitude of the coefficients of variables \({\textit{Drank}}{\_}\textit{2.5}^{*}{\textit{PIT-Drank}}{\_}\textit{4}^{*}PIT\).

  26. 26.

    Results do not significantly change if we decide to consider the conditional/conformity effect by using the other alternative variables considered in our estimates: GWR, ME-GROUP, CHEATED, RANK, WITHDRAW_LESS_THAN_MAX and WITHDRAW_MORE_THAN_MIN.

  27. 27.

    We repeat for a robustness check our estimates by creating a conformity/conditional cooperation variable in which we look at the difference between individual and group payoffs (and not individual and group withdrawal rates) and where we check whether inclusion/omission of the relevant individual in-group averages affects our findings. Results are unchanged and are available upon request.

  28. 28.

    Even though they obscure the impact of each time invariant regressor, fixed effects may be preferred if we believe that clustering standard errors is not enough to take into account the fact that we have repeated observations for the same individual. Furthermore, fixed effects have the additional desirable property of allowing us to control for unobservable time invariant socio-demographic factors. Even more important, fixed effects allow us to control for the experience lived by players during the first TG (see the end of Sect. 3), trustor’s contribution, trustee’s response and, in general, players’ satisfaction about the game, which is also invariant across CPRG rounds.

    Table 6 Determinants of players’ withdrawal rates (fixed effects)

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Acknowledgments

We are extremely grateful to James Andreoni, Sergio Beraldo, Tilman Brück, Jeffrey V. Butler, Alessandra Cassar, Luisa Corrado, Benedetto Gui, Luigi Guiso, Alberto Iozzi, Tullio Jappelli, Marco Pagano, Salvatore Piccolo, Fabiano Schivardi, Francesco Silva, Giancarlo Spagnolo, Daniele Terlizzese, Tommaso Valletti, Bruce Wydick, Luca Zarri, Alberto Zazzaro and all other participants in the seminars held at EIEF, CSEF, DIW, to the BELAB Conference and to the PRIN meetings for their useful comments and suggestions. We also thank Alice Cortignani and Alessandro Romeo for the invaluable research support in the field.

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Correspondence to Leonardo Becchetti.

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Becchetti, L., Conzo, P. & Degli Antoni, G. Public disclosure of players’ conduct and common resources harvesting: experimental evidence from a Nairobi slum. Soc Choice Welf 45, 71–96 (2015). https://doi.org/10.1007/s00355-014-0867-y

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JEL Classification

  • C93
  • Q20
  • H40