How Audits Moderate the Effects of Incentives and Peer Behavior on Misreporting

Abstract

Classical agency theory argues that economic incentives can have a strong impact on opportunistic reporting behavior. On the other hand, behavioral literature suggests that agents also adhere to descriptive norms established by peers. Most studies examine these effects in isolation, ignoring the role of mechanisms that firms use to detect misreporting. This research examines if the effects of incentives and descriptive peer norms depend on whether the firm uses an audit system to detect misreporting. In an experiment, we vary the material payoffs for lying (low vs. high compensation rate), the behavior of peers (low vs. high honesty), and the use of audits to detect misreporting (audited vs. not audited). Results indicate that the effect of peer behavior depends on the use of audits. When reporting decisions are audited, descriptive peer norms have a strong effect on the level of truthful reporting. We do not find evidence indicating that the effect of incentives depends on audits. Our findings have important implications for practice. Firms may need to consider the use of audits if they want to promote honesty through positive peer-established social norms.

Acknowledgements

This paper is based on Yuping Jia's dissertation at Tilburg University. Jia gratefully acknowledges the valuable suggestions from her dissertation committee, including Laurence van Lent (supervisor), Jan Bouwens, Peter Easton, and Holger Daske. We thank Henri Dekker (associate editor) and three anonymous reviewers for their helpful comments and suggestions. We also thank Margaret Abernethy, Bart Dierynck, Christopher Koch, Ranjani Krishnan, Anne Lillis, Joan Luft, and Michael Williamson for their helpful comments. We thank the workshop participants at Tilburg University, Mannheim University, Radboud University Nijmegen, and Free University Amsterdam, KU Leuven Research Day, the 2007 European Accounting Association Meetings, and the 2007 Annual American Accounting Association Meeting.

Funding

Yuping Jia acknowledges financial support from the Netherlands Organization for Scientific Research (project number 017.001.101).

Supplemental Data and Research Materials

Supplemental data for this article can be accessed on the Taylor & Francis website, http://dx.doi.org/10.1080/09638180.2015.1042889.

Notes

¹For example, the documentary The Smartest Guys in the Room on the Enron affair suggests that this firm was rife with unethical behavior. Dishonesty was the norm, and deviating from this behavior would have rendered an individual manager an outcast.

²Descriptive norms exist when individuals prefer a common pattern of behavior because they believe that most of their peers, defined as a group of similar people, follow that pattern as well (Bicchieri, 2006).

³Davidson and Stevens (2013) find that a code of ethics with public certification may activate social norms that reduce opportunistic behavior of managers.

⁴We conduct our experiment with a 2×2×2 design, as in practice companies use different incentive schemes in combination with audits. However, the three-way interaction of the audit, peer honesty, and incentive compensation is difficult to predict. Thus, we do not derive formal hypotheses for the three-way interaction but instead leave it as an empirical issue. As argued, theory posits that the presence of audits can affect (personal) norm perceptions of lying, which is important when discussing the differential impacts of peer honesty and incentives on the level of misreporting. Moreover, theoretical support for the interaction between peer honesty and incentives is not easy to derive, and we make no formal predictions here.

⁵We presume that this choice is more conservative because we feel it may bias against finding support for our predictions. If the headquarters would be another participant instead of a hypothetical company, then the setting becomes less anonymous and the effect of the audit is heightened. There may also be a stronger need to search for peer information when the setting becomes less anonymous (Kachelmeier & Shehata, 1994). Furthermore, the design allows us to also reduce the impact of alternative mechanisms for the effects we examine such as the incentive to appear honest, which occurs when the owner is another participant (Hannan et al., 2006). Such impression management occurs less against a hypothetical firm. In practice, participants often rationalize their misreporting against the company rather than to an individual (Evans, Moser, Newman, & Stikeleather, 2015).

⁶Given the available size of the participant pool, we introduce incentive compensation as a within-subject factor. In practice, it is not uncommon to change the incentive compensation package for the same manager across different investment projects (Shields & Waller, 1988). The limitation of introducing incentive compensation as a within-subject factor is that the treatment becomes salient. We, however, feel that this choice does not materially affect our inferences, as we are mainly interested in the potential moderating effect that audits have on incentives.

⁷We made this choice based on the observation that, in practice, internal auditors increase the likelihood to investigate the possible fraud if ‘income was greater than expected' (Church, McMillan, & Schneider, 2001). The choice of not disclosing the exact detection probability matters less in our design, as we are mainly interested in the effect of the presence or the absence of an audit. Disclosure of exact detection probabilities would matter more for investigating the effects of control system strength (e.g. Tayler & Bloomfield, 2011).

⁸If we let participants act on evolved norms during actual play, it may take longer for the descriptive norm to become sufficiently distinct. While percentages are set by the experimenter, the percentages are reasonable based on reporting behavior in the pilot test. Eight participants in a pilot test play the same 10 reporting rounds, alternating between incentive schemes without any audit or peer group information. If one combines the reports of the most honest participants, then a 75–90% rate of honest reports is reasonable. If one combines the reports of the most dishonest participants, then a 10–25% rate of honest reports is reasonable. Although these descriptive statements involve deception and may not represent a general pattern (which can be seen as a limitation), experimental economic studies use a similar approach to let people act on different descriptive norms (see Bicchieri & Xiao, 2009; Innes & Mitra, 2013).

⁹In practice, managers often receive information about their peers via internal benchmarking or disclosure of peer reporting behavior. Information policies also vary substantially from closed to open. Organizations with open policies share information about manager performance and pay. Organizations with closed policies might share information only at the aggregate level (Colella, Paetzold, Zardkoohi, & Wesson, 2007; Maas & Van Rinsum, 2013). Based on such information, managers might form their own beliefs about peer behavior. Even without such disclosures, employees still have their informal information channel. For example, a survey of 725 executives and managers indicates that 65% of the managers have personally observed or obtained direct evidence of one or more types of fraud, waste, or mismanagement within their company (Keenan, 2000). In practice, people may thus arrive at a rough estimate and may perceive that either a majority or minority of their peers is dishonest.

¹⁰As shown in Online Appendix 4, we measure social value orientation by having participants divide a hypothetical amount of money between themselves and a hypothetical other (Van Lange et al., 1997). Based on the most prominent choice, we classify participant types as (1) prosocial, or those with a high preference for joint outcomes; (2) individual, or those who prefer personal outcomes; and (3) competitive, or those who prefer a large positive difference between their own and other's outcomes. The individual and competitive types are classified as pro-self, consistent with prior research (Van Lange et al., 1997). We classify the participants into a type if they make the same type choice five out of nine times. Our sample contains 82 individual (53.9%), 24 competitive (15.8%), and 45 prosocial types (29.6%). One person, who could not be classified (0.65%), made four choices for the competitive type and four choices for the individual type and was therefore labeled as pro-self. Results are similar when we exclude this observation. We also use a more stringent definition and only classify a person if he or she makes the same choice six out of nine times (Van Lange et al., 1997). In this case, we lose more participants (n = 20), but the results remain qualitatively unchanged.

¹¹For practical reasons, the payment is rounded to the closest 50 euro cents.

¹²People who express more guilt or who perceive their actions to be more unfair to the firm also report more honestly (r = 0.340, p < .001; r = 0.196, p < .016). For the between-subject factor peers, we find no strong effects across the manipulation checks, presumably because statements about peers are always displayed to the participants (but they are manipulated to be honest or dishonest). However, their feelings of guilt increase slightly when other managers are honest (mean = 4.599 if peers are dishonest; 4.934 if peers are honest; F = 2.17, p = .07 one-tailed). For the factor incentive compensation, we cannot perform similar manipulation checks, because this factor is manipulated within subjects.

¹³An alternative dependent variable is the absolute size of the lie, measured as Y = actual (true) cost minus reported cost. Consistent with Brüggen and Luft (2011), we control for actual cost in the regressions. The covariate actual cost is significant, but the results (untabulated) do not qualitatively change. Subset analyses across audit conditions confirm that incentives maintain a strong effect on misreporting when audits are absent (at the 1% level), while peers have no significant impact. When audits are present, the effect of peers is highly significant (at the 1% level), while the effect of incentives decreases (significant at the 5% level in regressions without covariates and not significant in regressions including covariates). Alternatively, we can also add actual costs to the current regression results reported in the tables, with the honesty ratio as the dependent variable. Results (untabulated) do not qualitatively change.

¹⁴To get a complete picture, we also conduct descriptive analyses at the experimental round level. Descriptive statistics per experimental round show that, when auditing is absent, descriptive peer norms have no effect after the second round, under both the 10% and 50% incentive contracts. When auditing is present, however, descriptive peer norms seem to have an effect across all rounds, under both types of incentive contracts.

¹⁵Audits may also signal that uncooperative behavior is anticipated and ‘priced' (e.g. Gneezy & Rustichini, 2000). We do not see such crowding-out effects from the level of dishonesty at the report level. On the contrary, audits reduce the average level of misreporting, which is beneficial to firm profit. Nevertheless, when we repeat the analysis of Table 3 with a 0/1 dummy variable, which equals 1 if the report is fully honest (100% honesty) and 0 for any deviation from a truthful report, we find some crowding out as audits reduce the number of fully honest reports being produced (p < .01). Furthermore, none of the interaction variables concerning H1b and H2b are significant (all p’s > .325), but there are main effects of peers (at the 5% level when covariates are included) and incentives (at the 1% level). The effects of peer and incentive compensation are consistent with our main results. There are more fully honest reports when the descriptive norm is honest, relative to when it is dishonest. Also, more fully honest reports occur under the 10% incentive contract, relative to under the 50% incentive contract.

¹⁶To facilitate interpretations in Tables 3 and 4, we include only the covariates and their interactions with the main factors of interest. Besides theoretical reasons (see Section 3.2.4) there are operational reasons to include managerial type. Our randomization of participants across the between-subject conditions is largely successful (e.g. on accounting work experience, gender, etc.), except for managerial type. Results indicate that we have more prosocial type individuals in the audit-absent condition (mean = 0.36) compared to the audit-present condition (mean = 0.24). The difference across the two audit conditions are marginally significant (t = 1.66, p = .098). The covariates' gender and managerial type also have explanatory power, as univariate tests show that correlation between prosocial and honesty reporting is 0.07 (p = .064) under the 10% contract and 0.08 (p = .021) under the 50% contract; the correlation between gender and honesty reporting is 0.07 (p = .041) under the 10% contract and −0.11 (p = .003) under the 50% contract.

¹⁷We also check for end-trial effects, as participants may behave differently in the last experimental rounds (Hannan et al., 2006). The results, based on the data of the first eight rounds of play (removing the last alternation between the 10% and 50% contracts), are consistent with the results from the analysis of the 10 rounds of data. When end-trial effects are removed, ANOVA results using the average of the participant's reporting choices are consistent with results reported earlier. Specifically, when audits are absent, the main effect of peers is not significant (F = 0.04, p = .850), but incentives play a stronger role in the observed level of honesty (F = 7.77, p = .007); when audits are present, peer behavior becomes marginally significant (F = 3.95, p = .051). The effect of monetary incentives are not significant (F = 1.33, p = .252). If we include the covariates (ANCOVA), we find similar results with similar significance levels.

¹⁸An alternative explanation for the interaction between peer and audits (H1b) is that the degree of lying by peers conveys information about the accuracy of the audit system to the participants. We rule out this alternative explanation for two reasons. First, there is no punishment attached to auditing, so the accuracy of auditing should not matter to the participant in terms of psychological costs. Second, if this alternative theory holds, then we would expect to observe a trial effect (i.e. some learning of participants). We perform a formal test for trial effects on the interaction between trial × audits × peer, which is not significant (F = 1.25, p = .287).