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The effects of centralized power and institutional legitimacy on collective action

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Abstract

Most observed institutional arrangements, in governments, firms, and other organizations, acknowledge the effectiveness of imposing sanctioning institutions and monitoring policies to achieve particular goals. However, less attention has been paid to the influences of the delegation mechanism of sanctioning power. In particular, it remains unclear whether the mechanism influences the legitimacy of the authority/institution, in centralized institutional arrangements. We report laboratory-experimental results of a public goods game that compare the performance of exogenous (i.e., the Leviathan) versus endogenous (i.e., the Democracy) delegation of sanctioning power. Observed differences are not statistically significant, regardless of the effectiveness of sanctions imposed, tested in two experiments with different punishment/cost functions. Democratic schemes in centralized power environments should not be taken for granted. Experimental evidence contradicts the common belief of a robust causal relationship between indirect democratic institutions, collective action, and economic outcomes.

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Notes

  1. See Chaudhuri (2011) for a comprehensive review of this literature.

  2. The centralization of punishment per se does not guarantee higher efficiency. Dictators tend to overuse their power to achieve non-altruistic goals. Additionally, experimental studies found an ambiguity in the efficiency of centralized versus decentralized punishment arrangements. O’Gorman et al. (2009) and Carpenter et al. (2012) find contradicting results in public goods experiments, although differences in the designs might explain the results. For further discussion, see Van Lange et al. (2014).

  3. Recent efforts in this line of research include Andreoni and Gee (2012), Baldassarri and Grossman (2011), Grossman and Baldassarri (2012), Brandts et al. (2014), Carpenter et al. (2012), O’Gorman et al. (2009), and a summary of related literature in Van Lange et al. (2014). However, apart from Baldassarri and Grossman (2011) and Grossman and Baldassarri (2012), none of these studies focuses exclusively on the effects of the power delegation mechanism in a public goods game setting under sanctioning institutions and an incumbent punisher. Experimental designs typically involve other treatments that simultaneously affect contribution outcomes (e.g., leadership, information, and communication). See the next section for more discussion.

  4. In most institutional schemes observed outside the lab, the centralized punishment mechanism is costly to the society (e.g., bureaucracy and administrative costs involved in tax collection, and costs incurred on police and security infrastructure). Notably, our design adapts this feature by having an incumbent manager. The assigned punishment is costly for all group members, and the manager’s decisions are binding over everyone’s payoffs. For the sake of simplicity, the study does not consider institutional inefficiencies (e.g., corruption); hence, group members benefit equally from unassigned punishment.

  5. For an excellent review and summary, see Dal Bó (2014).

  6. Grossman and Baldassarri (2012) reaffirm the conclusions of the original study.

  7. For example, the manager’s perception on the level of inequality aversion might be stronger as an outside observer than as an inside manager.

  8. The intensity of reward and punishment varies in different experiments in the literature. For instance, Fehr and Gächter (2000a) use a strictly increasing and convex cost function. In Sefton et al. (2007), the ratio of cost for punisher and target is also 1:1. Nikiforakis (2008) provides a more cost-effective punishment, 3:1. Sutter et al. (2010) discusses the effect of intensity and compares the effectiveness with or without leverage, i.e., the ratio of 3:1 or 1:1. See the discussion in the survey by Casari (2005).

  9. Although this group number puts pressure on the sample size for statistical inference, it is the lowest (nontrivial) odd number that facilitates the manager’s selection process, particularly by reducing the chances of ties in the Democracy treatment.

  10. During the experiment, we subscribe to a neutral language and avoid the use of words such as “punisher,” “punishment,” and “tax.” Instead, we choose the following words: “manager,” “points reduced,” “points collected,” and “points assigned.”

  11. Note that, for ease of exposition, we interpret the punishment effectiveness ratio from the view of the number of points the group pays after the manager’s decision. A more standard approach, common in decentralized punishment environments, considers the number of points each player pays to reduce the punished subject’s payoff. For example, each player, including the manager, pays 1/5 (4 ECU) of the group account (20 ECU). If the manager decides to spend all points to punishing a free-rider, the group suffers a loss of 20 ECU; however, each player covers individually only 20% of the cost. As the punished individual still pays the tax, the punishment effectiveness is in the domain of 1:6. We thank an anonymous referee for this necessary clarification.

  12. We thank an anonymous referee for the suggestion to provide a numerical example.

  13. Consistency of the results can be tested under different tax/punishment and cost parameter calibration; we strongly encourage this practice in replication studies (Eckel et al. 2015).

  14. Throughout the experiment, we did not observe bankruptcy, since the punishment was typically assigned to the free-riders. Overall, the assigned punishment fluctuates in the whole range; however, 89% of the punishment assigned is no more than 10 points (mean\(=3.80\), median\(=0\)).

  15. Nikiforakis and Normann (2008) argue that “a punishment effectiveness of 3 or greater is required to obtain a welfare improvement compared to the public-good game without punishment.”

  16. One important precision. In the main experiment, the subjects in 6 sessions face a purely random selection process (instructions: ONE participant in your group will be randomly selected as a manager by the computer.), while the subjects in other 6 sessions were selected over the biased probability distribution mentioned (instructions: ONE participant in your group will be selected as a manager by the computer, based on a predefined distribution, unknown to you.). We calibrated the 75% probability based on the results observed in the Democracy treatment of the first sampling period. For the second experiment, the 75% probability applies to all sessions in the Leviathan treatment. Tables A3 and A4 in the Online Appendix provide statistical tests for differences in both samples. Consistent with the general results, estimates from the two samples are similar and both insignificant.

  17. We use a plurality voting rule without further restrictions for simplicity of exposition. This allows for circular voting; that is, each subject receives one vote. However, we did not observe this result. Additionally, we observed about 20% of ties during the main experiment, while no ties were observed during the second.

  18. Sample differences respond to administrative constraints.

  19. Subjects in the second experiment are from the Management School with no previous game theory training.

  20. No statistical significance is observed concerning the regression results when controlling for such differences. Further results are available upon request.

  21. The exchange rate was between 6.10 RMB (2013), 6.20 RMB (2015), and 6.7 RMB (2017) per USD 1.00, respectively, at the time of the experiments.

  22. Grossman and Baldassarri (2012) summarize similar arguments and related literature.

  23. Huber and Gordon (2004) argue that, under electoral accountability opportunities, judges become more punitive as reelection approaches. Our design does not allow for punisher’s reelection (see Castillo and Hamman 2020, for an extension); still, we expect some form of strategic behavior to come at play.

  24. The two-sided t-test reports similar results.

  25. Finding a non-significant effect is a relatively weak result, and we should be worried about the power of the test (\(1-\beta \)). For a conservative approach, given the small effect size, we calculate the power of the test of 0.63 (63%) in the main experiment. Although not ideal, due to known experimental challenges, we did not extend the sample size and relied on the stacked evidence from both experiments to reinforce the evidence. Both are reasonable samples that fall under standard experimental practices. We acknowledge this potential limitation.

  26. For example, exemplary punishment in the main experiment, applied to one subject with a group punishment distribution of: \(\left\{ 20, 0, 0, 0, 0\right\} \), can be more effective than a distribution of: \(\left\{ 5, 5, 5, 5, 0 \right\} \), possible in the second experiment; again, the average punishment points are the same in one round. We thank an anonymous referee for rising this important point.

  27. It is worth noticing that the effectiveness of punishment across treatments in the two experiments is not directly comparable. The two sequences in the example are possible in the second experiment, while the second sequence is not an option in the main experiment (for the group’s distribution case in one round). Also, the effect of the punishment sequence rises along with the group’s contribution behavior, among other confounding factors.

  28. Efficiency in this setting can also be measured in relation to potential earnings in each period (Eckel et al. 2010). Conclusions are the same.

  29. The identification strategy relies on the random assignment of the treatment. In other words, there are no systematic differences in the characteristics of participants between the control and treatment groups. In the context of laboratory experiments, the identifying assumption is satisfied (i.e., internal validity). Furthermore, the common trend assumption is satisfied; that is, there is no significant divergent trends between the two treatments in the first phase.

  30. Tobit panel regressions yield the same conclusions.

  31. Column 4 shows that managers may occasionally punish members who contribute even more than the average level in order to encourage all the group members to contribute as high as the highest level. This situation only happens in the starting period in the tax and punishment phase. The coefficient on positive deviation from the average contribution will be close to zero if we include all subjects instead of focusing only on the published subjects.

  32. The 10% significance disappears when we control for previous group performance. See the result in the Online Appendix.

  33. We thank an anonymous referee for highlighting this point, which motivated this section.

  34. In this literature, a leader has specific responsibilities and means to exercise their influence, for example, leading by example (e.g., others observe leader’s decisions); communication (e.g., sending encouraging messages); networks (e.g., by their location within a network); and leader’s social status (Ball et al. 2001; Eckel and Wilson 2007; Eckel et al. 2010; Kumru and Vesterlund 2010).

  35. Contribution levels are significantly higher for managers in the punishment phase of the democratic treatment, while contribution levels are the same among non-managers between treatments. This might falsely suggest that contribution incentives in the democracy are higher; that is, democratically elected managers feel a greater responsibility than managers imposed. Nevertheless, panel B accounts for within-subject differences among phases and destroys such suspicion. The increase in managers’ contributions in the tax/punishment phase is the same between the Leviathan and Democracy’s treatment.

  36. We thank a referee for suggesting this exercise. We report the analysis only for the main experiment. In the second experiment, 87.5% of the highest contributors within the group were selected. Hence, the comparison in the legitimacy level of the high contributors and other becomes meaningless in statistical power.

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Acknowledgements

We would like to thank Alex Brown, Catherine Eckel, Daniel Fragiadakis, Marco Palma, Charles Plott, Manfred Königstein, John Hamman and fellow members of the experimental research group at the Texas A&M University for their comments and support on this research. We acknowledge very constructive comments provided by anonymous referees. We would also like to thank the fellows at the 5th Antigua Experimental Economics Conference and the First LAWEBESS in Cali-Colombia, as well as fellows in the Café CIEC at FCSH-ESPOL. We are grateful to Jia Yan, Hongyu Guan and Wenjie Zhang for their outstanding laboratory support at SZU and NJUST. We also acknowledge the support by the National Natural Science Foundation of China (Project nos. 71703031, 71803136) and the Laboratory for Experimental and Behavioral Economics (L.E.E.) and the Research Funds (R-CD-FCSH-135-2017) of the College of Social Sciences and Humanities at ESPOL. This experiment obtained IRB approval from Shenzhen University and Nanjing University of Science and Technology. The informed consent was obtained from the subjects in this experiment. A previous version of this work circulated under the title: “Institutional Legitimacy and Public Goods Games: A Laboratory Experiment on the Distribution of Sanctioning Power.” The corresponding disclaimer applies. All errors are our own.

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Authors and Affiliations

  1. School of Social Sciences and Humanities, Escuela Superior Politécnica del Litoral-ESPOL, Guayaquil, Ecuador

    José Gabriel Castillo

  2. School of Economics, Henan University, 85 Minglun Street, Kaifeng, 475000, Henan, China

    Zhicheng Phil Xu

  3. China Center for Special Economic Zones, Shenzhen University, Shenzhen, China

    Ping Zhang

  4. School of Economics and Management, Nanjing University of Science and Technology, Nanjing, China

    Xianchen Zhu

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  1. José Gabriel Castillo
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Correspondence to Zhicheng Phil Xu.

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Castillo, J.G., Xu, Z.P., Zhang, P. et al. The effects of centralized power and institutional legitimacy on collective action. Soc Choice Welf 56, 385–419 (2021). https://doi.org/10.1007/s00355-020-01284-w

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