Abstract
We collect individual participant data from 70 papers that use laboratory experiments to examine individual tax evasion behavior (or “Tax Evasion Games”), in order to use meta-analysis to estimate the impacts of different public policy, experimental design and individual level variables on tax evasion choices. Our results show that standard enforcement variables like audits (including audit rules) and fines perform differently on the extensive and intensive margins. We find that other fiscal variables like a flat tax system, tax rates, and tax amnesties have unambiguous negative impacts on tax compliance, and that specific features of the experimental setting, such as how subjects are directed to report income, or whether taxes are redistributed to the participants or to a real life public good, have significant impacts on tax compliance. Our results also indicate that the demographic characteristics of the subjects (e.g., gender, experimental income, occupation, risk attitude) affect compliance.
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Notes
The evolution of the number of TEG published per year is shown in Fig. 2 in the "Appendix".
The estimated numbers of participants lost due to those collection problems is at most equal to 7835, which represents 102,191 individual subject decisions. However, these numbers are likely overestimates of the actual lost observations because many different articles have been published with a single dataset.
The collection output is featured in Fig. 3 in the "Appendix".
In principle, the tax system could of course be regressive as well. To our knowledge, there are no studies so far with a regressive tax system.
Simply dropping those observations does not change the conclusions from the main analysis of this article.
Those models are standard when it comes to analysing experimental data (e.g., Jacquemet et al. 2019) or meta-analyses data (e.g., Abeler et al. 2019). As discussed later, we have also estimated these specifications using a Logit model and a GLM model in Table 15 in the "Appendix", and our results are not affected. For the sake of transparency, we have also reported in Table 16 in the "Appendix", the average effect of the same variables using both Tobit and OLS models without distinguishing the extensive from the intensive margin of compliance.
Clustering at the individual level is standard because we are mostly dealing with individual-level decision making. As discussed later, we have also estimated these specifications with clustering at the study level in order to capture possible intra-study heterogeneity of compliance; see Table 11 in the "Appendix". Our results are unaffected. Another alternative would be to cluster at the session level. However, this information was not available in all the datasets of TEG that we gathered.
Country and Study Fixed Effects are an absolute necessity as the countries and the studies in which the TEGs were completed vary in their characteristics. In total, 19 countries are covered in our sample, spanning around 840 million world inhabitants (or about 11% of world population). These countries include: Albania, Australia, Austria, Belgium, Canada, Colombia, The Czech Republic, Denmark, France, Germany, Israel, Italy, The Netherlands, Romania, Slovakia, Sweden, Taiwan, the United Kingdom, and the United States. In majority, the participants in these TEGs are WEIRD (or White, Educated, Industrialized, Rich, and Democratic), and they probably do not represent the social preferences of the world population (Henrich et al. 2010). In addition, summary statistics from Table 8 in the "Appendix" show important discrepancies between countries in term of average compliance behavior. For example, the mean compliance rate in the TEGs conducted in these countries is 91% in Albania and 34% in Slovakia; the overall country average is 65%. We can only call for running more standardized TEGs in more different continents, especially in Asia, South America, and Africa.
From now on, unless otherwise stated, p values systematically correspond to t tests.
Note that this negative interaction holds mainly because of the presence of two countries that account for about 40 percent of the observations, or the USA and Italy (see Table 9 in the "Appendix").
There is also some evidence that higher audit rates can sometimes backfire, leading to lower post-audit compliance; that is, an audited individual may actually reduce his or her post-audit compliance, sometimes termed a “bomb-crater effect”. This effect is generally found in laboratory experiments in which tax compliance of audited taxpayers falls immediately after an audit (Mittone 2006; Maciejovsky et al. 2007; Kastlunger et al. 2009), before recovering somewhat in succeeding rounds. However, with some exceptions (Mendoza et al. 2017), field data generally find little or no evidence of a bomb-crater effect (Erard 1990). One explanation for the bomb-crater effect is that deterrence may “crowd out” an individual’s “intrinsic motivation” to pay taxes (Frey 1997), and a similar finding has been found in field data for corporate taxpayers (DeBacker et al. 2015). Other explanations are that individuals may update their subjective audit probabilities following an audit, that they may attempt to “restore” their income following an audit, or the audit may alter their perceptions of the efficiency of the tax administration (Mittone et al. 2017). There is also some experimental work that finds that delayed feedback on tax audits is more effective in improving compliance than immediate feedback, possibly because delay leads individuals to overweight audit probabilities (Kogler et al. 2016). This issue remains unresolved.
However, the relatively low number of studies implementing a progressive tax system might affect the generalizability of this conclusion. Some other variables such as redistribution of the tax fund could interact with the progressivity of the tax system. Table 13 in the "Appendix" shows that, when public policy and experimental variables are pooled, the effects of having a flat tax and redistribution exist, but their interaction is not very useful because there is only one dataset that implements a progressive tax system without redistribution. We can only suggest that there is need for more experiments with non-standard experimental settings, such as varying the progressivity along with the redistribution of the taxes.
The impact of income does not change when we consider an income eliminating the differences in price levels between countries, see Table 10 in the "Appendix" where Income has been replaced by Income (PPP).
Table 11 in the "Appendix" features the impact of risk attitude pooled with the public policy variables on lab tax compliance. The results still show a somewhat positive impact of risk aversion on both margins.
The information above is summarized in Table 12 in the "Appendix". Note that the average number of observations that could be considered as risk averse varies widely across methodologies, ranging from 27% in SQ1 and PC to 87% in Dospert.
The treatment of risk attitudes yields different general results in both laboratory and field experiments (see e.g. Friedman et al. 2014; Galizzi et al. 2016; Charness et al. 2019). It poses challenges in experimental economics, for several reasons. First, because of the relatively small stakes used in most experiments, risk aversion is inconsistent with expected utility theory, as demonstrated by Rabin (2000), who concludes that “...within the expected-utility model, anything but virtual risk neutrality over modest stakes implies manifestly unrealistic risk aversion over large stakes” (pp. 1281–1282). Second, from the perspective of behavioral economics, testing for risk aversion is problematic because, relative to the reference point, many individuals are risk-averse or risk-neutral in gains but risk-seeking in losses (Kahneman and Tversky 1979). As a result, risk preference may depend on whether decisions are framed as gains or losses, and methods for testing risk aversion do not typically test for framing effects. Third, the experiments that we examine involve many rounds, and risk preferences may change over rounds since repeated market experience can induce framing effects (Coursey et al. 1987; List 2003). However, methods for testing risk aversion do not typically consider that risk preferences might change with experience. Finally and relatedly, these methods do not consider how risk preferences might change with, say, framing effects or with the weighting of high and low probabilities. For all of these reasons, a single measure of risk aversion is not likely to be a useful concept in the experimental studies that we examine because these experiments typically have modest stakes, include both gains and losses, employ multiple rounds with changing subject experience, and use probabilities of audit that imply different weights relative to actual probabilities of audit.
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Acknowledgements
We thank John D’Attoma, Duccio Gamannossi Degl’innocenti, Miguel Fonseca, Xavier Gassmann, Nicolas Jacquemet, Matthias Kasper, Stéphane Luchini, Daniele Nosenzo, Salmai Qari, Alessandro Santoro, the participants to the MUEES, TARC, Augustin Cournot, ADRES, Maastricht, Budapest, ESA, Lille seminars and all the researchers who contributed to this meta-analysis. We also thank three anonymous reviewers along with Ragan Petrie and Marie-Claire Villeval. The dataset generated in this meta-analysis is not publicly available as data are property from their respective authors. The dataset can be obtained on request, after express authorization from the authors who did not make their data available online.
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Appendix
Appendix
Evolution of number of TEG per year
Status of the different articles featuring a TEG
First invitation to contribute
Reminder email
See Tables 6, 7, 8, 9, 10, 11, 12, 13, 14, 15, 16 and 17.
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Alm, J., Malézieux, A. 40 years of tax evasion games: a meta-analysis. Exp Econ 24, 699–750 (2021). https://doi.org/10.1007/s10683-020-09679-3
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DOI: https://doi.org/10.1007/s10683-020-09679-3