Sie können Operatoren mit Ihrer Suchanfrage kombinieren, um diese noch präziser einzugrenzen. Klicken Sie auf den Suchoperator, um eine Erklärung seiner Funktionsweise anzuzeigen.
Findet Dokumente, in denen beide Begriffe in beliebiger Reihenfolge innerhalb von maximal n Worten zueinander stehen. Empfehlung: Wählen Sie zwischen 15 und 30 als maximale Wortanzahl (z.B. NEAR(hybrid, antrieb, 20)).
Findet Dokumente, in denen der Begriff in Wortvarianten vorkommt, wobei diese VOR, HINTER oder VOR und HINTER dem Suchbegriff anschließen können (z.B., leichtbau*, *leichtbau, *leichtbau*).
The literature on experimental tax and regulatory compliance has highlighted significant advantages associated with competitive audit selection mechanisms (ASMs) predicated on differences in estimated undeclared incomes among taxpayers. This paper explores the potential negative consequences of competitive ASMs in situations where authorities lack an unbiased indicator of these differences. Through a laboratory experiment, we demonstrate that asymmetric information between taxpayers and tax authorities can diminish compliance and exacerbate inequality within competitive ASMs. Our findings underscore the need for caution concerning the perceived benefits of competitive ASMs and emphasize the importance of allocating resources to mitigate income heterogeneity among groups subject to competitive audit selection.
This financial support from the Czech Science Foundation through Grant 17-00496S is gratefully acknowledged. The article was prepared within the framework of the Basic Research Program at HSE University.
Publisher's Note
Springer Nature remains neutral with regard to jurisdictional claims in published maps and institutional affiliations.
1 Introduction
Audits are the primary means tax and regulatory agencies have at their disposal to increase compliance. A higher frequency of audits has been shown to increase compliance in the laboratory (Alm, 2012; Alm et al., 1992) as well as in field settings (Dwenger et al., 2016; Fellner et al., 2013; Kleven et al., 2011; Meiselman, 2018; Slemrod et al., 2001). However, increasing the frequency of audits is costly and tax authorities seek to target reports that exhibit suspicious patterns (Santoro et al., 2023). An alternative approach is thus to collect additional information on taxpayers’ income (Gilpatric et al., 2011; Kuchumova, 2017; Menichini & Simmons, 2014). Such information improves the authority’s ability to estimate true taxable income and target audits toward taxpayers with the largest discrepancies between reported and estimated income.
For instance, in the case of emissions regulations, the enforcement authority is responsible for monitoring compliance within a group of firms, which are similar in their characteristics but still heterogeneous in the level of emission. The authority can measure ambient pollution to obtain an unbiased estimate of each plant’s actual emissions, while also observing the emissions reported by firms. By taking advantage of this information, the enforcement authority can rank the regulated agents according to their estimated levels of non-compliance and then select them for audits according to this rank. In the context of tax compliance, the tax authority may segment taxpayers into different cohorts by occupation, firms’ size, address or other observable characteristics. Taxpayers in the same cohort would have similar income, and the tax authority could rank them by their declarations. In practice, however, heterogeneity within peer groups limits the accuracy of such relative rankings, often leading to the misidentification of low-income taxpayers as non-compliant. To address this, the authority can invest in additional information—for instance, by cross-checking declarations against third-party reports—which provides signals about true income and enables more precise targeting of audits toward the most non-compliant taxpayers. Acquiring such signals is inevitably costly, and it is not clear whether the benefits outweigh the cost.
Anzeige
In this paper, we use a laboratory experiment to evaluate the benefits of acquiring a noisy yet unbiased signal of true income and conducting subsequent audits based on that signal. In particular, our experiment simulates a situation where the tax authority creates cohorts of taxpayers with similar actual income. Although the tax authority may know the distribution of income in the cohort, it does not observe taxpayers’ actual income due to individual income shocks. The audit selection mechanism (ASM) ranks taxpayers in the cohort by their declared income and selects for audit those with the lowest declaration. We compare the outcomes of such ASM with an one where the tax authority can make use of signals of individual income shocks and with a random ASM in which all taxpayers face equal audit selection probability.
This paper relates to the theoretical literature on information reporting and optimal audit policy (Kuchumova, 2017; Macho-Stadler & Pérez-Castrillo, 2002; Menichini & Simmons, 2014), which emphasizes that acquiring signals about taxpayers’ income enhances audit targeting and promotes tax compliance. Contributing to this line of research, the present paper experimentally evaluates the efficiency of two ASMs: one based on signals of true income and another relying solely on the ranking of reported income within a peer group. This comparison provides new insights into the benefits of acquiring income signals for improving audit effectiveness.
It follows from theoretical literature that optimal ASM targets audits to taxpayers who report low income (Sanchez & Sobel, 1993) or low income conditional on the signal (Kuchumova, 2017). Previous experimental studies have shown that such ASMs, also called competitive ASMs, are powerful tools for increasing tax and regulatory compliance without increasing the number of audits (Bayer, 2019; Cason et al., 2016; Gilpatric et al., 2011). The paper addresses the specific information requirement of the ASMs thus far proposed in the literature. Gilpatric et al. (2011) assume that the auditors possess noisy, but unbiased, information about taxpayers’ individual income shocks1; Colson and Menapace (2012) assume the existence of informative output measures for a subgroup of firms; and Alm and McKee (2004) suppose that the tax office has sufficient information to divide the taxpayers into subgroups with identical incomes. These ASMs are based on the assumption that the tax authority acquires signals that perfectly explain income heterogeneity, or at least that the residual income heterogeneity is purely random and unknown to the taxpayers. Such signals might be unavailable or too costly to acquire. As a result, incomes will be heterogeneous in any group that the tax office is able to select and taxpayers will obtain an informative signal about how their income compares with their peers’ income. Taxpayers with higher income may thus exploit this information to pay lower taxes, which may undermine the efficiency of competitive ASMs and increase income inequality. We contribute to the literature on competitive ASMs by looking at the implications of income variation that is known to taxpayers but unobserved by the tax authority.
Competitive ASMs based solely on declared, rather than undeclared, output were studied theoretically by Bayer and Cowell (2009) and Oestreich (2015, 2017). They show that these competitive audit mechanisms lead to higher tax compliance. In these models, the taxpayers choose the actual output first and then decide how much to declare. In deriving our theoretical predictions, we follow a model similar to the declaration stage in the model by Bayer and Cowell (2009) and Oestreich (2015). Our model departs from theirs in two key aspects. Although both frameworks assume that taxpayers have an informational advantage over the tax authority, their model takes this assumption to the extreme by granting taxpayers complete information about one another’s output. In contrast, we assume that taxpayers know only their own output (income) but do not observe other taxpayers’ output. Moreover, their solution is based on the symmetric Nash equilibrium concept, which means that output is homogeneous on the equilibrium path. Our model differs in that output is exogenous and heterogeneous by assumption. We examine the properties of competitive ASMs under income heterogeneity unobserved by the tax authority or, more generally, when the subjects are heterogeneous in the variable they are supposed to report. Our theoretical model shows that the competitive ASM, in which the audit probability depends only on the declared incomes, leads to higher compliance than an ASM with an exogenously given audit probability.
Anzeige
As explained above, tax authorities do not have to possess all income-relevant information available to taxpayers. However, they may at some cost gather more data to form more precise estimates of actual income and reduce its informational disadvantage. In order to gain insights about the effects of more precise income signals on performance of the competitive ASM, and provide a benchmark which is closer to the environments studied thus-far in the literature, we consider a situation in which tax authorities obtain information about each individual’s realized income. We find that this signal, which effectively eliminates auditor’s informational disadvantage, further increases compliance.
We also calculate total revenue, which depends not only on tax receipts from declared income, but also on fines from audits. This points to a stark difference between the competitive ASM with and without this signal: assuming equilibrium strategies, when audit probabilities depend only on declared incomes, poorer taxpayers are more likely to be audited than richer taxpayers, while the opposite is true when an estimate of income is incorporated. However, our theory shows that any change in fines due to auditing is outweighed by increased tax revenues, and predicts that both competitive ASMs increase total revenue compared to the random ASM, and more so when information regarding true income is available.
Finally we also consider the theoretical impact of ASMs on inequality. Clearly inequality is reduced when a signal of income is used, because of greater compliance and the increasing relationship between income and probability of audit. However, when only declared income is used, the impact of greater compliance is muted by more frequent auditing of the poor. Despite this countervailing force, inequality is predicted to be reduced under both competitive ASMs, with a greater reduction when a signal about income is utilised.
These predictions are tested using an economic experiment. We propose a design in which all taxpayers receive income that is drawn from a uniform distribution. Their task is to choose the declared income which is then taxed at a fixed rate. They may be selected for audit with a particular audit probability. Subjects who are selected for audit and declare less than their income pay a penalty. The experiment has three treatments that differ in the way the audit probability is determined: an ASM where all taxpayers are audited with the same exogenously given probability (random); a competitive ASM based on declared income (no-signal); and a competitive audit selection mechanism which makes use of a signal of true income (signal). The no-signal treatment corresponds to a real-world application of a competitive ASM in which some income heterogeneity in the cohorts is inevitable, while the (signal) treatment represents a benchmark situation where the tax authority obtains noisy but unbiased signals of individual income shocks. In the treatments with a competitive audit selection, the subjects are divided into groups of five taxpayers. In no-signal, the audit probability decreases with the difference between each subject’s declared income and the average declared income of the other four subjects in their group, whereas in signal, it increases with the difference between the subject’s (estimated) undeclared income and the group average.
In line with the theoretical predictions we find that, in comparison to random ASM, compliance is significantly improved on average by using the no-signal competitive ASM based solely on declared income, and more so by additionally utilizing noisy information about true income in the signal competitive ASM. We also find the predicted relationship between income and audit probability with poorer taxpayers audited more often in no-signal and less often in signal. So while revenue is increased and inequality decreased in signal, the positive impacts in these respects in no-signal are small and statistically insignificant.
2 Experimental design
2.1 Treatments
In this section we describe the experimental task and treatments, and state our hypotheses. The more general theoretical framework on which the experiment is based, and the proofs underlying our hypotheses, are contained in Online Appendix B.
At the beginning of each round, each taxpayer i receives income \(I_i\), which is drawn from a uniform distribution between 0 and 200 CZK. The task of each taxpayer is to choose a declared income \(R_i \in \left[ 0, I_i \right] \). This declared income is taxed at a rate \(\tau = 0.6\). Taxpayers who are selected for audit and declare less than their income, pay a penalty equal to their undeclared income \(I_i-R_i\).2 Thus, a taxpayer receives \(0.4R_i\) if audited, and \(0.4R_i + (I_i - R_i) = I_i - 0.6R_i\) if not selected for audit.
The experiment consists of three treatments which differ in the way that audit probabilities are calculated. In the treatment with the random ASM (random), the audit probability of each taxpayer i is \(\pi _i = 0.4\). The audit probabilities for the remaining two treatments have a form of the relative difference contest success function (Beviá & Corchón, 2015). They resemble closely the generalized audit selection rule proposed by Gilpatric et al. (2011), and are chosen such that the expected number of audits is the same in all three treatments.
2.1.1 Signal treatment
In the treatment with the competitive ASM where the tax authority has access to a noisy estimate of actual taxable income (signal), taxpayers interact in groups of five. Each taxpayer’s audit probability is increasing in the difference between their undeclared income and the average undeclared income of the other four taxpayers. We emphasize here that we are not requiring that the auditor knows the true income, which would clearly make auditing unnecessary: this mechanism can be considered a reduced form for a situation where the tax authority knows not only the expected income of peer-group members, but also has a noisy signal of each individual’s income shock, and always audits a fraction of those with the highest estimated undeclared incomes. The randomness of the selection function stands in for the noisiness of the signal.
We now illustrate this derivation for the two-person case. Taxpayer \(i \in \lbrace 0,1\rbrace \) gets income \(I_i=M+\gamma _i\), where M is the expected income of the peer-group and \(\gamma \) is the taxpayer-specific income shock. Each taxpayer knows their income \(I_i\). Each taxpayer then decides how much to declare, \(R_i \le I_i\). The tax authority obtains signal of taxpayer’s income \(S_i=M+\gamma _i+\epsilon _i\) where \(\epsilon _i\) is an i.i.d. draw for each taxpayer from the distribution G representing the error in estimating actual income.3 The tax authority audits the taxpayer with the highest estimated undeclared income, \(S_i-R_i\). The probability of being audited is
where \(H(\cdot )\) is the cumulative distribution function of the random variable \(\epsilon _i-\epsilon _j\). So, the probability of being audited is the cumulative distribution function evaluated at the difference between actual undisclosed incomes.
As in Gilpatric et al. (2011), we test a more general form of the competitive audit mechanism, where the probability of being audited is a function of the difference between i’s declaration and its actual income and average of this difference in the peer group. In particular, the audit probability we implement in this treatment is
where \(Z_i=I_i-R_i\) is the undeclared income and \(R_{-i}\) stands for the incomes of the four remaining members of the group.4 The error term \(\epsilon \) is not explicitly mentioned as it is implicitly captured by the formula. The reason we chose not to model the noisy signal explicitly is to keep our two competitive audit treatments (especially the experimental instructions) as close as possible, while still capturing the essential features of the two information environments.
2.1.2 No signal treatment
Returning to the two-person case, suppose now that the tax authority knows only M, and each \(\gamma _i\) is known only by the taxpayers. In this case, the taxpayers can be ranked only on the cruder estimate of undeclared income, \(S_i=M+\epsilon _i\). The probability of being audited is therefore
Note that this probability follows exactly the same functional form as in signal, but is evaluated at the difference between declared rather than undeclared income. The treatment with the competitive ASM with no signal regarding taxable income (no-signal) is therefore identical to signal, with the exception that in the formula defining the random ASM, undeclared income is replaced with declared income:
Using the results from Online Appendix B, we can now derive equilibrium strategies for the parameters used in the experiment. Declared income in random is zero. In no-signal, declared income should be one half of the actual income, \(R_i=I_i/2\). In signal, declared income is zero when the actual income is below 40 and each additional income above 45 is fully declared, i.e. \(R_i=\max \{0,I_i-45\}\). The average declared incomes in the random, no-signal and signal treatments are 0, 50 and 60.1, respectively. This calculation gives us our first hypothesis:
Hypothesis 1
Average declared income in signal is higher than in no-signal. The average declared income in no-signal is higher than in random.
However, the comparison of the average declared incomes does not tell the whole story. Figure 1 shows how the theoretically predicted declared income depends on actual taxable income. It demonstrates that the effects on individuals of different ASMs depend on the levels of taxpayers’ actual incomes. Taxpayers with incomes lower than 90 CZK are expected to comply more fully in no-signal. On the other hand, taxpayers with higher income should declare more in signal. Following this prediction about declared income, we can formulate our second hypothesis:
Fig. 1
Equilibrium strategies based on experimental parameters
For low income levels, declared income will be higher in no-signal than signal. For medium- and high-income levels, declared income will be lower in no-signal than signal.
Figure 2 sheds further light on the difference between low- and high-income individuals. The figure depicts the relationship between equilibrium audit probability5 and income level. In no-signal, the lack of information about each individual’s income mean that high-income individuals are audited with lower probability. In signal, the ASM is based on undeclared incomes, which results in constant audit probabilities. Only the taxpayers with incomes below 45 CZK are audited with lower probability, which reflects that they are constrained by the lowest possible declared income of zero. The relationship shown in Fig. 2 gives us our third hypothesis:
Fig. 2
Relationship between expected audit probability and income
The probability of being audited is decreasing in income in no-signal and weakly increasing in signal.
Total revenue comes from two sources: tax declarations and fines from failed audits. Income from declarations is purely a function of declared income, so if Hypothesis 1 is correct, this will be highest in signal, and lowest in random on average. Income from fines on the other hand, depends not only on the proportion of income declared by individuals who are audited, but also on the probability with which each taxpayer is audited. According to Hypothesis 3, in signal richer people should be audited more frequently than in random, mitigating the reduction in audit revenue due to lower tax declarations, whereas in no-signal, poorer people are being audited, exacerbating the reduction in audit revenue. Nevertheless, in theory, the net effect of both competitive ASMs is to increase total revenue. Table 1 shows the total revenue by treatment, assuming the parameters implemented in our experiment. These are reflected in the following hypothesis:
Hypothesis 4
Total revenue is highest in signal, and lowest in random.
With respect to inequality in net income, there are again countervailing effects. In signal, inequality is reduced by both the steeper relationship between income and declared income, and the fact that richer people are audited more frequently. In contrast, in no-signal, the reduction in inequality relative to random due to higher declarations is counterbalanced by the fact that poorer people are more often audited. The predicted Gini coefficients obtained through simulation of net income for our experimental parameters are shown in Table 1, and they lead to the formulation of our final hypothesis:
Hypothesis 5
The variance in post-tax income is lowest in signal, and highest in random.
Table 1
Predicted revenue and inequality
Signal
No-signal
Random
Expected revenue
52.54
46.63
40
Gini coefficient
0.438
0.487
0.680
2.3 Procedures
The experiment was conducted at MUEEL in Brno, Czech Republic, in 2017 and 2018. The subjects were mostly students and recruited through hroot (Bock et al., 2014). The experiment was programmed in zTree (Fischbacher, 2007). We used neutral instructions, i.e. the tax motivation of the game is not clear from the instructions (the instructions were in Czech language—an English translation is provided in Online Appendix C). We ran 11 sessions using a between-subjects design. In particular, we ran three sessions for random for which each subject was considered to be one independent observation, four sessions for no-signal where groups of five were considered to be one independent observation and four sessions for signal where again each group of five was considered an independent observation. The total number of participants was 200, with no less than 15 participants per session. Each session consisted of 30 rounds with partner-matching, and lasted almost 90 min. The subjects received payments based on five randomly selected rounds. The mean payoff was 240 CZK (approx. 9 EUR, a little more than twice the average student wage).
At the beginning of each experimental session, an experimenter read the instructions aloud, with the subjects (taxpayers) following along with their copy. Subjects were asked to answer control questions in order to reinforce comprehension of the instructions before the experiment. To avoid the risk of anchoring, the questions did not include any particular numbers. All numerical inputs were entered by subjects themselves.
3 Results
3.1 Data
The dataset consists of observations from the 200 participants, each of them playing 30 periods, individually or as part of a group for 6,000 observations in total. We filter out the 18 observations in which the income is \(I = 0\) because, under those circumstances, the subjects had no opportunity to evade taxes. As it is standard in similar experimental literature founding their predictions on equilibrium models, we do not use data from the early rounds in the analysis to allow subjects to learn e.g., (Gilpatric et al., 2011). In particular, we use the data only from the last 15 rounds. As a robustness check, all results were estimated using all 30 periods. The results remain the same, or at least very similar, in terms of statistical as well as economic significance (the main regression results estimated using all 30 rounds are reported in Online Appendix A).
Table 2 displays the descriptive statistics for the selected variables for the three treatments. The table includes choice and outcome variables as well as socio-demographic variables. There are fewer subjects in random since, in that case, each subject is considered as an independent observation, whereas a group of five constitute an independent observation in the other two treatments. This follows a standard experimental practice in which participants’ behavior in later rounds of a partner-matching protocol is not treated as independent, given the feedback received in previous rounds. Although our sample is not balanced in terms of gender, this should not bias the results since we control for personal characteristics in the regressions.6 Approximately one half of the subjects were students of economics or business. Some of our subjects had previously participated in other economics experiments, but they had not participated in a similar tax compliance experiment.
Table 2
Descriptive statistics
Signal
No-signal
Random
Subjects
80
75
45
Groups (independent observations)
16
15
45
Income
97.64
101.21
100.70
Declared income
70.88
63.49
52.91
Expected total revenue
55.42
52.51
50.86
Standard deviation of final payoff
28.55
38.51
42.49
Female
0.38
0.49
0.60
Age
22.18
23.08
21.53
Students of economics or business
0.48
0.45
0.42
Note Average values
3.2 Declared income
As can be seen in Table 2, and in line with Hypothesis 1, average declared income was 70.88, 63.49, and 52.91 in the signal, no-signal, and random treatments, respectively. Column 1 in Table 3 shows the result of linear regressions of declared income on treatment dummies (no-signal is the baseline), which shows that the difference between random and both competitive ASMs are statistically significant (\(p<0.001\) for signal, and \(p=0.034\) for no-signal); the difference between the two competitive ASMs is weakly significant (\(p=0.077\)).7 As shown in the second column, controlling for income increases the average difference between signal and no-signal to almost 10, and raises the level of statistical significance (\(p=0.011\)). As shown in the third specification, these results are robust to controlling for gender, age, and field of study, none of which are statistically significant.
Hypothesis 2 relates to the different predicted relationships between income and declared income across the treatments. Given the non-linear nature of our prediction for signal (see Fig. 1), we begin by estimating nonparametric kernel regressions of declared income on income separately for each of the three treatments. As can be seen in Fig. 3, and as hypothesized, the slope of the estimated relationship is steeper for signal than no-signal, with declared incomes lower in the former treatment for low incomes, and higher for high incomes. Contrary to the theoretical prediction, declared income rises with income in random which can be explained by risk-aversion.8 To keep things parsimonious, and as our nonparametric regressions suggest that all three relationships are close to linear, we estimate a linear regression allowing for different slopes in the different treatments to assess the statistical significance of these observed differences. This is reported in column 4 of Table 3. All differences of slopes and intercepts between all three treatments are highly significant (\(p<0.01\)), with the exception of the slopes of random an no-signal, which do not differ. Controlling for gender, age, field of study, and whetever the individual was audited in the previous period does not alter any of the conclusions in this section (column 5 and 6).
Fig. 3
Relationship between declared income and actual income (nonparametric kernel regression—optimal bandwidth selected using improved AIC)
The model specification in column (6) indicates that being audited leads participants to report lower income in the subsequent period, potentially reflecting a belief that they are less likely to be audited again soon. This result is consistent with the bomb-crater effect documented in previous laboratory experiments (Maciejovsky et al., 2007; Mittone et al., 2017). In contrast, field studies typically find the opposite pattern, whereby taxpayers become more compliant following an audit (Hebous et al., 2023; Advani et al., 2023). The apparent discrepancy between our findings and those from field settings may be reconciled by Christiansen (2024), who show that intentional non-compliers exhibit little behavioral response to audits, whereas audits promote higher compliance among individuals who make inadvertent errors—an aspect likely absent in laboratory environments.
Table 3
Declared income—rounds 16–30
(1)
(2)
(3)
(4)
(5)
(6)
Signal
7.634+
9.908*
9.498**
− 15.92***
− 16.67***
− 17.01***
(4.253)
(3.775)
(3.580)
(1.739)
(1.761)
(1.765)
Random
− 10.54*
− 10.27*
− 11.59*
− 8.070*
− 9.537**
− 9.940**
(4.870)
(4.591)
(4.497)
(3.298)
(3.342)
(3.285)
Income
0.698***
0.697***
0.598***
0.597***
0.594***
(0.0267)
(0.0268)
(0.0294)
(0.0294)
(0.0295)
Signal # Income
0.260***
0.262***
0.266***
(0.0377)
(0.0380)
(0.0378)
Random # Income
− 0.0222
− 0.0225
− 0.0191
(0.0598)
(0.0593)
(0.0591)
Female
1.783
1.774
1.778
(2.610)
(2.555)
(2.540)
Age
− 0.704
− 0.820+
− 0.785
(0.494)
(0.488)
(0.482)
Economics student
− 1.154
− 1.143
− 1.168
(2.338)
(2.317)
(2.295)
Audit in \(t-1\)
− 4.626***
(1.202)
Constant
63.60***
− 7.118*
8.839
2.940*
21.67+
23.06+
(2.891)
(3.030)
(11.77)
(1.436)
(11.79)
(11.60)
Observations
2990
2990
2990
2990
2990
2990
\(R^{2}\)
0.019
0.654
0.655
0.676
0.678
0.680
OLS regressions with robust standard errors clustered at the group level. Observations, where income \(I = 0\), are excluded. +\(p<0.1\), *\(p<0.05\), **\(p<0.01\), ***\(p<0.001\)
3.3 Audit probabilities
The third hypothesis is also confirmed by experimental data. Figure 4 displays the predicted values of nonparametric regressions of audit probability on income, estimated separately for the signal and no-signal treatments. We can see that the estimates correspond closely to the theoretically predicted relationship (Fig. 2). A probit regression of audit probabilities on a treatment dummy, income, and the interaction, find that audit probabilities are negatively related to income in no-signal (\(p<0.01\)), positively related to income in signal (\(p=0.019\)), and that the difference in these relationships is statistically significant (\(p<0.01\)), with all standard errors clustered at the group level.9
Fig. 4
Relationship between audit probabilities on actual income (nonparametric kernel regression—optimal bandwidth selected using improved AIC)
In this section we focus on expected total revenue, i.e. the expectation of revenue calculated on the basis of audit probabilities implied by actual declarations, rather than on the basis of actual audit realizations. This removes the noise associated with the randomness in audit selection, and allows for more precise estimation of treatment effects. As reported in Table 2, and in line with Hypothesis 4, average revenue was 55.42, 52.51, and 50.86 in the signal, no-signal, and random treatments, respectively. Table 4 displays the results of OLS regressions on revenue, with the same specifications as for declared income.10 Regressing only on treatment dummies shows that revenue is significantly higher in signal than the other two treatments, but no-signal does statistically no better than random. Controlling for income only increases the magnitude and statistical significance of the advantage of the ASM in signal.
When allowing for interaction effects between the treatment and income (column 4), the results are very similar to those for declared income. Note, however, that unlike with declared income, the relationship between revenue and income in random is steeper than in no-signal, reflecting the decreased number of audits on richer taxpayers in the latter treatment. Again, controlling for demographics does not alter any of these conclusions (column 3 and 5).
Table 4
Expected total revenue—rounds 16–30
(1)
(2)
(3)
(4)
(5)
(6)
Signal
3.093*
4.825***
5.048***
− 10.47***
− 10.30***
− 10.32***
(1.346)
(0.629)
(0.608)
(0.728)
(0.712)
(0.715)
Random
− 1.590
− 1.384
− 1.462
− 7.356***
− 7.533***
− 7.553***
(1.843)
(0.942)
(0.934)
(0.742)
(0.750)
(0.748)
Income
0.531***
0.531***
0.456***
0.456***
0.456***
(0.0116)
(0.0116)
(0.00887)
(0.00886)
(0.00888)
Signal # Income
0.153***
0.153***
0.154***
(0.0103)
(0.0104)
(0.0104)
Random # Income
0.0588***
0.0590***
0.0592***
(0.0137)
(0.0137)
(0.0136)
Female
1.436**
1.444**
1.444**
(0.513)
(0.485)
(0.486)
Age
0.0526
0.000390
0.00213
(0.0957)
(0.0881)
(0.0880)
Economics student
− 0.247
− 0.266
− 0.267
(0.520)
(0.518)
(0.518)
Audit in t-1
− 0.232
(0.289)
Constant
52.60***
− 1.268
− 3.095
6.330***
5.725**
5.795**
(1.026)
(1.171)
(2.523)
(0.445)
(2.095)
(2.112)
Observations
2990
2990
2990
2990
2990
2990
\(R^{2}\)
0.004
0.938
0.939
0.954
0.954
0.954
OLS regressions with robust standard errors clustered at the group level. Observations, where income \(I = 0\), are excluded. +\(p<0.1\), *\(p<0.05\), **\(p<0.01\), ***\(p<0.001\)
3.5 Inequality
We measure the inequality through the Gini coefficient of net income within a group and period. Subjects from random are randomly distributed to virtual groups of five to maintain comparability with the other two treatments. The theoretical Gini coefficient of ex-ante income is 1/3 for a uniform income distribution (0 to 200). The Gini coefficient of net income was 0.293 in signal, 0.347 in no-signal, and 0.363 in random. The regressions in Table 5 show that inequality is significantly lower in signal, while no-signal and random do not differ significantly from one another. These results remain unchanged when controlling for the Gini coefficient of gross income and for demographic characteristics.
Table 5
Inequality (Gini coefficient of net income)—rounds 16–30
(1)
(2)
(3)
Signal
− 0.0543***
− 0.0630***
− 0.0663***
(0.0111)
(0.00994)
(0.00992)
Random
0.0164
0.0117
0.0198
(0.0171)
(0.0165)
(0.0148)
Income
0.603***
0.599***
(0.0393)
(0.0389)
Female
− 0.0358
(0.0230)
Age
0.00191
(0.00476)
Economics student
0.0415+
(0.0233)
Constant
0.347***
0.182***
0.137
(0.00815)
(0.0127)
(0.111)
Observations
600
600
600
\(R^{2}\)
0.074
0.384
0.391
OLS regressions with robust standard errors clustered at the group level. Observations, where income \(I = 0\), are excluded. +\(p<0.1\), *\(p<0.05\), **\(p<0.01\), ***\(p<0.001\)
4 Discussion and conclusion
Earlier competitive ASMs have been based on the assumption that the enforcement authority has noisy, but unbiased, information about each individual’s output. While only restrictive in some settings, this assumption is clearly unrealistic in the tax compliance setting.
In this paper, we study the effect of this assumption on outcomes of competitive ASMs. Using experimental methods, we show that an ASM in which the audit selection is based solely on declared income (no-signal) leads to higher tax compliance than a random mechanism in which all taxpayers are audited with the same baseline probability. In particular, we show that the mechanism works even if the incomes of the taxpayers in the reference group differ substantially. Furthermore, the mechanism is designed in such a way that the expected number of audits is kept constant, which means that the additional cost of implementing the mechanism consists only of the administration of the more complex audit selection procedure. In sum, our paper suggests that the competitive ASM might be an affordable and effective tool for reducing tax evasion under constraints of real-world tax collection where the tax office does not have information about the actual income of taxpayers.
However, the desirability of this mechanism is limited by the fact that low-income taxpayers in the reference group are audited more frequently. This may be difficult to justify from a social justice point of view. Moreover, it has a countervailing effect on the increase in tax revenue and decrease in inequality engendered by greater compliance. In contrast, a comparison with our benchmark ASM in which a signal of true income is available shows that not only can such information increase compliance, but more frequent auditing of the rich further increases revenue and reduces inequality. This calls into question the size of the benefits of ASMs found thus-far in the literature, in the more realistic case of residual asymmetric information between taxpayers and tax authorities about the ranking of true incomes. Additionally, even though an unbiased signal of the actual income may not be available in a real-world setting, it would be not only fiscally worthwhile to spend up to the resulting increase in revenue in obtaining more homogeneous groups of reference taxpayers, but the social value of the additional information may be even greater if inequality reduction is an objective.
It is also important to note that the inequality effects observed in our experiment arise from income differences within the reference groups used for audit selection. In practice, tax administrations have substantial third-party information—such as employer-reported income, withholding statements, and other information returns—that enables them to construct relatively homogeneous strata before audits are performed (Fellner et al., 2013; Kleven et al., 2011; Slemrod et al., 2001). This stratification substantially reduces the misclassification of taxpayers and limits the scope of distortions within the group (Kuchumova, 2017; Macho-Stadler & Pérez-Castrillo, 2002; Menichini & Simmons, 2014). Because stratification minimizes most variation between taxpayers, the inequality effects we identify pertain only to residual heterogeneity within otherwise homogeneous groups. Our design deliberately abstracts from this preliminary step to isolate the mechanism by which misclassification can still arise despite extensive third-party information. Thus, the findings illustrate the existence and direction of this mechanism, rather than implying that its practical magnitude reflects inequality throughout the income distribution. Many significant components of the tax base—such as self-employment income, small business activities, rental income, and other items not included in third-party reporting—are still not subject to enforced information flows. As a result, competitive ASMs can still have a substantial impact on revenue in these areas.
Finally, we would like to note that although we did not find significant improvements in total revenue and inequality when only declared income influenced audit probabilities, we consider this is secondary to the robust effect on individual behavior. This substantial increase in compliance suggests that for larger samples, a statistically significant increase in revenue and reduction in equality may be found, although the issue of excessive targeting of the poor for audits would remain.
Declarations
Conflict of interest
The authors declare no conflict of interest.
Open Access This article is licensed under a Creative Commons Attribution 4.0 International License, which permits use, sharing, adaptation, distribution and reproduction in any medium or format, as long as you give appropriate credit to the original author(s) and the source, provide a link to the Creative Commons licence, and indicate if changes were made. The images or other third party material in this article are included in the article’s Creative Commons licence, unless indicated otherwise in a credit line to the material. If material is not included in the article’s Creative Commons licence and your intended use is not permitted by statutory regulation or exceeds the permitted use, you will need to obtain permission directly from the copyright holder. To view a copy of this licence, visit http://creativecommons.org/licenses/by/4.0/.
Publisher's Note
Springer Nature remains neutral with regard to jurisdictional claims in published maps and institutional affiliations.
In the experiment in Gilpatric et al. (2011) the signal is not explicitly mentioned, however it exists implicitly because the experiment implements the special case where all subjects have the same income.
In the notation of Online Appendix B, this results from setting \(\phi =1\). Note that this formulation is equivalent to a case where the taxpayer pays a fine which is equal to underreported tax times a fine rate \(1/\tau \).
The sensitivity of the function with respect to differences in declarations (0.004) was chosen as a compromise between making it large enough to make significant differences, but remain within the unit interval.
As a further check, we ran regressions of declared income on a gender dummy for the combined data, and separately by treatment: the point estimate in the combined data indicated that females declared 1.5 less than males; in no case did we find a statistically significant relationship.
By the first-order condition, the marginal rate of substitution between income in the no-audit and audit states equals \(\pi (1-\tau )/((1-\pi ) \tau \)). Since income in the audit state does not depend on the initial income, the reported income must increase with initial income for risk-averse decision makers.
For our regressions for revenue, we continue to use individual data rather than aggregating to the group level. This is necessary to allow us to control correctly for income, because the non-linearity in predicted treatment differences mean that for some realizations of income levels, the sign of the predicted average treatment difference between signal and no-signal can reverse if group income predictions are incorrectly based on average group income, rather than averaging after predictions are made at the individual level.
Advani, A., Elming, W., & Shaw, J. (2023). The dynamic effects of tax audits. Review of Economics and Statistics,105(3), 545–561.CrossRef
Alm, J. (2012). Measuring, explaining, and controlling tax evasion: Lessons from theory, experiments, and field studies. International Tax and Public Finance,19(1), 54–77.CrossRef
Alm, J., Jackson, B., & McKee, M. J. (1992). Estimating the determinants of taxpayer compliance with experimental data. National Tax Journal,45(1), 107–114.CrossRef
Alm, J., & McKee, M. (2004). Tax compliance as a coordination game. Journal of Economic Behavior & Organization,54(3), 297–312.CrossRef
Bayer, R., & Cowell, F. (2009). Tax compliance and firms’ strategic interdependence. Journal of Public Economics,93(11), 1131–1143.CrossRef
Bayer, R.-C. (2019). The double dividend of relative auditing—theory and experiments on corporate tax enforcement. School of Economics and Public Policy Working Papers 2017-14, University of Adelaide, School of Economics and Public Policy.
Beviá, C., & Corchón, L. C. (2015). Relative difference contest success function. Theory and Decision,78(3), 377–398.CrossRef
Bock, O., Baetge, I., & Nicklisch, A. (2014). hroot: Hamburg registration and organization online tool. European Economic Review,71, 117–120.CrossRef
Cason, T. N., Friesen, L., & Gangadharan, L. (2016). Regulatory performance of audit tournaments and compliance observability. European Economic Review,85, 288–306.CrossRef
Christiansen, T. G. (2024). Dynamic effects of tax audits and the role of intentions. Journal of Public Economics,234, Article 105121.CrossRef
Colson, G., & Menapace, L. (2012). Multiple receptor ambient monitoring and firm compliance with environmental taxes under budget and target driven regulatory missions. Journal of Environmental Economics and Management,64(3), 390–401.CrossRef
Dwenger, N., Kleven, H., Rasul, I., & Rincke, J. (2016). Extrinsic and intrinsic motivations for tax compliance: Evidence from a field experiment in germany. American Economic Journal: Economic Policy,8(3), 203–32.
Fellner, G., Sausgruber, R., & Traxler, C. (2013). Testing enforcement strategies in the field: Threat, moral appeal and social information. Journal of the European Economic Association,11(3), 634–660.CrossRef
Fischbacher, U. (2007). Z-Tree: Zurich toolbox for ready-made economic experiments. Experimental Economics,10(2), 171–178.CrossRef
Gilpatric, S. M., Vossler, C. A., & McKee, M. (2011). Regulatory enforcement with competitive endogenous audit mechanisms. The RAND Journal of Economics,42(2), 292–312.CrossRef
Hebous, S., Jia, Z., Løyland, K., Thoresen, T. O., & Øvrum, A. (2023). Do audits improve future tax compliance in the absence of penalties? evidence from random audits in norway. Journal of Economic Behavior & Organization,207, 305–326.CrossRef
Kleven, H. J., Knudsen, M. B., Kreiner, C. T., Pedersen, S., & Saez, E. (2011). Unwilling or unable to cheat? evidence from a tax audit experiment in denmark. Econometrica,79(3), 651–692.CrossRef
Kuchumova, Y. P. (2017). The optimal deterrence of tax evasion: The trade-off between information reporting and audits. Journal of Public Economics,145, 162–180.CrossRef
Macho-Stadler, I., & Pérez-Castrillo, J. D. (2002). Auditing with signals. Economica,69(273), 1–20.CrossRef
Maciejovsky, B., Kirchler, E., & Schwarzenberger, H. (2007). Misperception of chance and loss repair: On the dynamics of tax compliance. Journal of Economic Psychology,28(6), 678–691.CrossRef
Meiselman, B. S. (2018). Ghostbusting in Detroit: Evidence on nonfilers from a controlled field experiment. Journal of Public Economics,158, 180–193.CrossRef
Menichini, A. M. C., & Simmons, P. J. (2014). Sorting the good guys from bad: on the optimal audit structure with ex-ante information acquisition. Economic theory,57(2), 339–376.CrossRef
Mittone, L., Panebianco, F., & Santoro, A. (2017). The bomb-crater effect of tax audits: Beyond the misperception of chance. Journal of Economic Psychology,61, 225–243.CrossRef
Oestreich, A. M. (2015). Firms’ emissions and self-reporting under competitive audit mechanisms. Environmental and Resource Economics,62(4), 949–978.CrossRef
Oestreich, A. M. (2017). On optimal audit mechanisms for environmental taxes. Journal of Environmental Economics and Management,84, 62–83.CrossRef
Sanchez, I., & Sobel, J. (1993). Hierarchical design and enforcement of income tax policies. Journal of public economics,50(3), 345–369.CrossRef
Santoro, A., Spinelli, D., & Berta,P. (2023). Retrieving tax audit criteria to estimate tax audit impact. SSRN.
Slemrod, J., Blumenthal, M., & Christian, C. (2001). Taxpayer response to an increased probability of audit: Evidence from a controlled experiment in minnesota. Journal of Public Economics,79(3), 455–483.CrossRef
