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Debiasing preferences over redistribution: an experiment

Abstract

We study the manipulation of preferences over redistribution. Previous work showed that preferences over redistribution are malleable by the experience of success or failure in a preceding real-effort task. We manipulate the information subjects receive about the importance of chance relative to effort in determining success. We investigate the effect of this manipulation on (1) subjects’ redistribution choices affecting third parties, and (2) preferences for redistributive taxation. Our results show that informing the subjects about the relative importance of chance after the real-effort task does not mitigate the self-serving bias in redistribution choices. Only providing full information before the real-effort task prevents the emergence of the self-serving bias.

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Notes

  1. Weinzierl (2017) provides survey evidence showing that respondents do not seek full equalization of unequal outcomes produced entirely by randomness.

  2. A related strand of literature studies similar effects in bargaining (Gächter and Riedl 2005; Karagözoğlu and Riedl 2015), dictator games (Erkal et al. 2011; Spiekermann and Weiss 2016), money burning (Fehr 2018), and effort provision (Kovárík et al. 2018).

  3. In few sessions of the PostTask treatment, participants were not given this last piece of information, namely that the game was designed such as randomness almost completely determined success. We found no statistical difference neither for the demand of redistribution in the DDG (\(p=0.806\), Wilcoxon rank-sum test), nor in the RTG (\(p=0.652\)), and we pool these observations for the remainder of the paper.

  4. The associated redistribution choices were: 0%, 9.1%, 18.2%, 27.3%, 36.4%, 45.5%, 54.5%, 63.6%, 72.7%, 81.8%, 90.9%, 100%. We deliberately excluded the 50-50 split (as e.g. in Bellemare et al. 2008).

  5. We slightly depart from the DDG introduced in Deffains et al. (2016) in three ways. First, we do not display the difference of tokens between the two targets, but let dictators choose on a percentage of redistribution. This ensures that all dictators have the same strategy space. Second, we make the consequences of the dictator’s decision highly salient by means of the graphical representation. Third, participants do not learn their payoff at the end of the DGG, which minimizes spillovers on the subsequent game.

  6. The second series of tasks consisted in memorizing pictures and short video clips. After displaying each picture or video clip for about one minute, subjects had to answer questions regarding their contents. For this second real-effort task there was no hard/easy manipulation and no median split of the participants according to performance. The sole purpose of the second real-effort task was to generate variance in the earnings among subjects in a group to render the choice over redistribution in the RTG meaningful.

  7. After the random dictator mechanism participants were asked to bargain within their group of four to reach a consensus on the redistribution rule. The bargaining process consisted of five stages, in each of which participants could publicly announce their desired level of redistribution, and bargaining would stop in case of unanimous agreement on a tax rate. Both the random dictator and the result of the bargaining were potentially relevant for the outcome of the RTG. With 50% probability a group’s final tax rate was determined by the random dictator rule; with the remaining probability it was determined by the bargaining. In the following we will focus on the private decision, as this is not confounded with strategic concerns.

  8. The fact that we observe switchers raises the question whether our design was deceptive, because we told subjects that would be virtually impossible to switch. At the time we designed the experiment we based the wording of the instructions on observations from four sessions of our previous work (Deffains et al. 2016), where we used the same real effort task and observed perfect separation. We decided to keep the procedures constant between sessions despite the fact that we observed switchers in the experiments for the present study. In addition, the instructions read virtually impossible, which technically still concedes the possibility of switching.

  9. We compute scores of standardized performance by centering and standardizing the performance scores at the session and task level.

  10. To fully capture the treatment effect, we rely on an instrumental-variable approach such as suggested by Angrist et al. (1996). To do so, we instrument the actual treatment (overachiever or underachiever group) by the intention to treat (easy or hard task assignment). The instrumented variable overachiever is no longer correlated with the error term (due to the composition effect), because the task assignment was randomly allocated.

  11. Results available upon request.

  12. All regressions exclude targets from the disinterested dictator game.

  13. The coefficient associated with overachievers for Baseline loses in significance. Results available upon request.

  14. All regression results are available on request.

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Acknowledgements

We thank the seminar participants in Leuven (CELSE), Rennes (CREM), Hué (PET), and Paris (AFSE). Financial support of the Institut Universitaire de France is gratefully acknowledged.

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Correspondence to Christian Thöni.

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Espinosa, R., Deffains, B. & Thöni, C. Debiasing preferences over redistribution: an experiment. Soc Choice Welf 55, 823–843 (2020). https://doi.org/10.1007/s00355-020-01265-z

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