Adults in the room? The auditor and dividends in small firms: evidence from a natural experiment

The level of dividends is a key decision managers make in small- and medium-sized private firms. Dividends reflect a trade-off between compensating owners and maintaining firm liquidity and capitalization. Dividends are also a key variable of interest to policy makers concerned about how financial and accounting regulation may distort firm behavior. The finance and accounting literatures recognize the importance of dividends both as a primary mechanism for compensating shareholders (Baker and Wurgler 2004), and as a costly signaling mechanism from firm managers to outside stakeholders about the financial condition of a firm (Easterbrook 1984; Miller and Rock 1985; Allen et al. 2012).

Arguably, the long-term interests of a private firm and its stakeholders and the short-term preferences of a manager may not always be aligned, even if the manager has a considerable ownership stake. Since equity shares of private firms can be difficult to sell, a cash-constrained owner wishing to extract liquidity from a firm can do so mainly through a dividend payout (Bauwhede et al. 2015).¹ Even in the small firms where the manager is the sole shareholder, conflicts could arise between the manager and outside stakeholders such as tax authorities and vendors. Auditors have the purpose of ensuring the completeness, validity, and accuracy of transactions as reflected on firm financial statements. In this role, they can influence how a manager balances the trade-off between dividends and retained earnings.

In this article, we hypothesize that auditors of private, small- and medium-sized firms constrain dividends by promoting accounting conservatism. The managers and owners of small firms often do not have formal accounting or financial training. Auditors are expected to maintain independence in relation to a firm’s strategy and operations, and by law they are not allowed to perform a bookkeeping role. But they do have a duty to report issues with the firm’s going concern, such as liquidity and financial robustness. They can also communicate weaknesses in the firm’s accounting and internal control processes (Downing and Langli 2019). In other words, the auditor can play the role of the financial adult in the room. By pointing out weaknesses in a firm’s accounting reports and explaining conservative accounting principles, the auditor can impose a degree of financial discipline on small firms. All else equal, accounting conservatism has the effect of reducing current earnings (Watts 2003), which in turn constrains dividends (Smith and Warner 1979; Smith and Watts 1992; Leuz 1998; Louis and Urcan 2015; Bradford et al. 2017).

The “adults in the room” hypothesis is not ex ante obvious. An extensive literature in accounting explores the relationship between accounting quality and access to financing. In this mechanism, the auditor can be assumed to improve the quality of the financial accounts. In turn, this can be expected to lessen principal–agent problems of asymmetric information between firms and external lenders. If retained earnings is a substitute for bank and equity financing, then a reduction in accounting quality due to the absence of an auditor may lead to higher dependence on retained earnings and in turn a lower dividend. Recent research by Downing and Langli (2019) finds that firms that opt out of an audit tend to have lower-quality financial reports, as measured by a lower compliance quality score.

To our knowledge, this mechanism of auditor impact is under-explored in the literature. Anecdotally, auditors we have spoken to see this mechanism as plausible for small firms. Small firms often see auditors as financial authority figures. The literature that does exist also seems to provide support for the hypothesis. Manson et al. (2001) study management letters by auditors among unlisted companies and find that auditors often provide advice on appropriate accounting methods and policies.

In this article, we make use of Norwegian register data on small private firms and a recent implementation of an audit exemption policy for firms under given size thresholds to measure the effect of auditing on dividends. The policy shock is important since accounting conservatism can be difficult to measure directly (Chy and Hope 2021), and accounting conservatism may be endogenous to the process of determining dividends.

The identifying assumption in our article is that the threshold value for the exemption can be considered arbitrary within a narrow range of firm sizes. Whether a firm is just under or over the threshold can then be considered random. The introduction of this policy can be seen as a natural experiment, with a treatment group (i.e., those not being required to obtain an audit) being randomly assigned. This forms the heart of our identification: Comparing firms just below and above the thresholds to estimate an effect of auditing on dividends. We relax the assumption of random assignment by controlling for indicators of firm size and risk as well as by creating a balanced synthetic control with propensity score matching.

With the inclusion of several variables for firm characteristics, the methodology becomes a regression discontinuity. The estimate of the effect of auditing is obtained by measuring the jump, or discontinuity, at the policy threshold in relation to the overall trend of the size variables. We obtain estimates from specifications with both linear and nonparametric smoothed functions of the size variables. As a robustness check, we estimate difference-in-difference parameters that control for unobserved time-invariant variables.

We find a statistically and economically positive effect of audit exemption on dividends. A firm with operating revenues at the threshold of the exemption policy is estimated to increase their dividend by on average 35,000–85,000 NOK (or approximately €3700–9000). These estimated average magnitudes are significantly higher than the typical cost of auditing a small firm in Norway. Auditing costs for small firms can vary widely, though a report for the Norwegian Ministry of Finance from 2008² estimates an average cost of around 15,000–20,000 NOK. A report by Langli (2015) estimates average cost savings of approximately 14,000 NOK. Thus, the estimates likely reflect a real change in firm behavior rather than just a shifting of saved auditor costs. To put these magnitudes in perspective, the average firm in our sample had operating revenue of approximately 6.7 million NOK. Relative to revenues the average estimated change in dividends is modest, representing only between 0.5 and 1.2% of the operating revenues of a business. However, the mean dividend in our sample was approximately 136,000 NOK. The estimated change in dividends as a percentage of average dividends is substantial.

Our contribution is threefold. First, we contribute to the policy discussion of audit exemption policies. We find that the absence of an auditor leads to an economically meaningful change in firm behavior in the form of increased dividends in small private firms. Second, we add to the literature on accounting conservatism by providing evidence that auditing has the effect of promoting conservative accounting practices and imposing a degree of financial discipline on small private firms that may lack financial sophistication. Finally, we apply the modern theory and methodology of causal modeling with the Rubin (1974) potential outcomes approach to a current topic within the accounting and auditing literature. The use of such methodologies within accounting research has become increasingly prominent, and this article provides another case study.

In the next section, we discuss the institutional setting of our study, including a review of the theoretical mechanisms connecting auditing with dividends in private firms. In Sect. 3, we describe the data and provide descriptive statistics. Section 4 provides a discussion of the assumptions necessary for a causal interpretation of our results and related challenges. Section 5 describes the regression discontinuity design and presents results. Section 6 extends the regression discontinuity model to include a matched control group that provides improved balance. Section 7 discusses results from a difference-in-difference estimation as a robustness check. Section 8 concludes with a summary of the results and implications.

While Norway is not an EU member, it is a member of the European Economic Area. Norway is bound to most European accounting and auditing laws and standards established by 4th and 7th European commission directives (“the accounting directives”) from 1978 and 1983. Norway is also a small open economy, where external trade makes up a large portion of GDP and where many firms have foreign customers, suppliers, investors, and owners. Norwegian auditing standards are largely in line with those from the International Standards of Auditing (ISA) (Downing and Langli 2019).

Norway has some institutional features that differentiates it from other countries. Much of the literature on auditing in private firms uses data from Anglo-Saxon countries, with a tradition for common-law judicial systems and relatively high litigation risk. Norway has a civil judicial system more in line with much of continental Europe, with lower litigation risk. This could in theory affect auditor independence, as the threat of litigation is sometimes seen as a check on auditors breaching their obligation of independence. But a study by Hope and Langli (2010) failed to find evidence for breaches of auditor independence in Norway.

The audit exemption rule was implemented in Norway as a part of a larger policy of reducing the bureaucratic and administrative costs to firms, especially small firms and start-ups. This policy goal was codified into law, requiring the government to reduce the bureaucratic costs of conducting business by at least 3 billion NOK per year. The audit exemption was the largest component of this policy, with an estimated cost reduction of 2 billion NOK per year (Langli 2015).

Most EU countries have long traditions for audit exemptions. Table 1 shows thresholds for the Nordic countries as well as the UK. Small countries tend to have correspondingly small threshold values compared to the UK. Norway’s thresholds were set to a maximum balance sheet of approximately €2 million (20 million NOK) and a net turnover of approximately €500,000 (5 million NOK), and no more than 10 employees.³ In some countries, the audit exemption thresholds coincide with thresholds associated with other policies. To our knowledge, the thresholds in Norway are only used for purposes of determining whether a firm qualifies for an audit exemption.

The threshold conditions for the Norwegian policy are cumulative, meaning that all conditions must be met before a firm can forgo auditing. To issue the proxy, a two-thirds majority of the votes and share of the capital represented at the annual general meeting is required.⁴ Status in any given year is determined from the previous year’s financial results. The thresholds are “hard”, meaning that they are not adjusted for firms that move across them from 1 year to another.

Norway is an interesting case study because it is a late adopter of the audit exemption policy. The UK, for example, already introduced an audit exemption in 1994 (Collis et al. 2004). By contrast, the Norwegian policy was rolled out first in 2011. Audits can be a significant expense for small- and medium-sized firms. Kausar et al. (2016) estimate that an audit can cost 6% or more among private small- and medium-sized European firms. Because Norway has had an auditing requirement for all firms up until 2011, a competitive market for audit services has developed with transparent pricing. Thus, we can compare our estimated magnitudes to reasonable estimates of the cost of obtaining an audit.

Our data is from the Norwegian Centre for Corporate Governance research database, which consists of all Norwegian firms for the sample period (2010–2015). We limit the sample to firms that were active during the entire period 2005–2015. This limits the sample to 27,126 unique firms. We remove micro-firms, with revenues or total balance of less than NOK 500,000 (approximately €50,000). We do not filter based on the number of employees since after filtering on revenues and assets, no firms had large deviations from the threshold on number of employees. We removed firms that do not report revenues, inventory, account receivables, or accounts payable each year in the sample period. Some industry groups are not eligible for an audit exemption and have not been included. This includes public limited corporations, financial firms, law firms, foundations, lottery firms, drugstores, and accounting and auditing firms. After these exclusions, we are left with 5293 firms. We also remove firms with revenues of over NOK 15 million and a total balance of over NOK 50 million. We are left with 3025 unique firms. Finally, the remaining firms are checked against the official Norwegian firm registry (“Brønnøysundsregistrene”), leaving 2866 firms.

We loosen the assumption of random treatment assignment by controlling for a host of variables. Firm size is important as it signals that; (i) managerial ownership normally decreases with increased firm size and (ii) there may be fixed costs associated with starting an audit relationship, which will be relatively smaller for larger firms (Chow 1982; Fama and French 2001; Sharma 2011). We measure firm size as both total assets and operating revenue. These variables also determine eligibility for the audit exemption. By controlling for firm size in both the treatment and control groups, we measure the discontinuity at the threshold rather than the average difference between groups. Given the importance of controlling for firm size between treatment and control groups, we present results with both linear controls and nonparametric smoothed controls for firm size.

Agency theory suggests that high-risk firms are less likely to pay dividends, as they tend to have reduced access to capital markets and need to be self-financed to a higher degree (Ho 2003). We measure firm risk as the standard deviation of the return on assets (ROA), where ROA is defined as earnings before interest and taxes plus interests, divided by total assets.

According to the Jensen (1986) free cash flow hypothesis, higher cash holdings should be related to higher dividend payouts. Cash flow is measured as the sum of operating income and depreciation. We include firm mean cash flow across the years 2011–2015 in our analysis. Since cash flow uncertainty may constrain dividends, the standard deviation of cash flow is also included.

The profitability of a firm is important in determining the dividend. However, we consider the reported income to be a post-treatment variable and co-determined with dividends, an issue we discuss below. But we do include lagged operating income as a control variable.

Leverage may also influence the propensity to pay dividends, as firms must ensure that they have sufficient liquidity to meet short- and long-term obligations. We measure leverage as total debt divided by total assets.

Finally, we control for sector- and year-fixed effects in the analysis. Table 2 shows the names and descriptions of the variables included in the regressions.

Table 3 presents summary statistics for the variables used in the analysis. Statistics are calculated from firm-year observations from 2011 to 2015, which are the years in our sample where the audit exemption was instituted. Many firms pay out 0 in dividends at least some years. By design, all firms have significant amounts of revenue; however, some firms have years with negative operating income. There is a wide range for both leverage and return on assets, but the 25th and 75th percentile statistics show that most firms lie within a much narrower range. Finally, the proportion of firms in a year that are eligible and choose to forgo an audit is 14% of the total.

Figure 1 shows correlations among the variables of interest. A star within a square indicates a correlation coefficient that is statistically significant at the 95% confidence level. Notably, the correlation coefficient between operating income and dividends is relatively high at approximately 0.50, though this is not statistically significant. The correlation between dividends and operating revenues, total assets, and number of employees, which are used as thresholds for the auditor exception rule, are substantially lower.

Eligibility for the exemption policy is established by way of three thresholds: Operating revenue, total assets, and number of employees. Figure 2 shows a scatter plot of all the firms in our data by operating revenue and total assets. The red lines represent the policy thresholds for firm size. Orange dots represent firms that chose to forgo auditing in that year. The policy had not been implemented yet in 2010, and only a limited roll-out happened in 2011. 2012 was the first year with a full roll-out, where all firms under the thresholds could forgo an audit. The figure makes clear that in most cases the binding constraint for eligibility is operating revenue. The number of firms who come under the operating revenue threshold but over the total assets threshold is as little as two firms (2012–2014) and at most four firms (2015). Thus, the effect of total assets as a binding constraint is negligible.⁵

A concern is that firms are intentionally adjusting their operating revenue to come just below the threshold. A recent literature finds evidence for such strategic manipulation of reported firm size to avoid disclosure or auditing Bernard et al. (2018). In our case, strategic size management may be particularly concerning since manipulating accounting data to come under the thresholds is contrary to conservative accounting practices and might introduce a bias in our estimation.

Identifying size management is straight forward. If such manipulation exists, then it should have the effect of creating a discontinuity at the threshold, as those just over the threshold have an incentive to manage their accounts downward. We focus on the operating revenue threshold, as it is binding for most observations. Figure 3 shows histograms of operating revenue before and after the implementation of the policy, with vertical black lines representing the threshold values. The limits of the x-axis are constrained to values close to the threshold. If firms were acting strategically in response to the exemption policy, we would expect to see “bunching” of frequencies just below the threshold after the implementation of the policy. No pattern of bunching is apparent.

We use a regression discontinuity approach to identify the effect of an audit exemption on dividends. The identifying assumption is that the threshold set for defining what firms are small enough to forgo an auditor is arbitrary within a narrow range of firm size.

We can first consider a theoretical scenario where an experimental randomization can be performed. In the case of random assignment to a control and treatment groups, unobserved variables that might otherwise bias the results satisfy the criteria of ignorability (Rubin 1974). Using the notation of Imbens and Rubin (2015), we let \(Y_{i1}\) represents the potential outcome if the firm, i, is not audited, and \(Y_{i0}\) represents the potential outcome if firm i is in the control group, which is audited. Treatment, in this case, is the introduction of the auditing exemption, represented by \(T_i=1\). Given randomization, the average treatment effect can be estimated as in Eq. 2. In other words, the claim is that the randomization gives the possibility to make an estimation from a counterfactual: The difference in the dividend pay-out of a given firm i under both a scenario where they are, and are not, audited.A complication for our case is that it is not auditing itself that is randomized, but rather the option to be exempt from auditing. The quantity of interest then becomes the Average Treatment Effect for the Treated (ATT), as in Eq. 3. In words, this is the average difference in the dividend payout of a given firm i who is not audited (\(Y_{i1})\) with the counterfactual of the same firm that obtains an audit (\(Y_{i0}\)), given the introduction of an audit exemption (\(T_i=1\)).We have several reasons for being interested in the ATT versus the pure average treatment effect. The first is that a pure treatment effect is impossible to estimate if firms had a choice of whether to forgo an auditor. From a policy evaluation perspective, it is also the ATT effect that is relevant. The counterfactual scenario of all firms under the threshold forgoing an auditor is not of particular interest in evaluating a policy where firms are in fact given the choice of whether to obtain an auditor.

A problem with the ATT as written in Eq. 3 is that the counter-factual \(E(Y_{i0}|T_i=1)\)—the outcome for the treated observations if they did not receive the treatment—cannot be directly observed. The problem is that we do not observe which firms above the threshold would have forgone an auditor if given the choice (quadrants III and IV in Fig. 4). If the entire group above the threshold is used as a control, then this could confound the results. In particular, the estimation may pick up on a signal and screening effect. Since an exemption policy makes choosing to get audited observable, this can be used as a signal to stakeholders about the company’s financial situation. In a similar fashion, since audits are costly, choosing to get audited can have a screening effect, with high-quality firms willing to pay the auditing cost to demonstrate their financial robustness independent of the effect of the actual financial reports (Kausar et al. 2016).

In attempting to estimate the real financial reporting effects of an audit, we compare those firms that chose not to obtain an audit with a control group that was above the threshold and thus was required to obtain an audit. The firms that voluntarily chose to be audited are excluded. The key empirical challenge in this article is controlling for the factors that affect whether a firm above the threshold would choose to forgo an audit if they could.

Including control variables can help alleviate the potential bias that may be introduced by this self-selection but may not be sufficient to make the sample balanced between the treatment and control. Therefore, we also use propensity score matching to create a synthetic control group with improved balance.

By making use of the full panel of our data and a difference-in-difference identification strategy, we can also control for unobserved variables that may be correlated with treatment assignment. Instead of only comparing above and below the threshold after the introduction of the exemption policy, we compare changes in firms’ dividend between the years directly before and after the introduction of the policy and then compare average changes between firms in the treatment and control groups. In this way, unobserved variables that are correlated with the treatment but that are time-invariant are differenced out. The difference-in-difference strategy comes at the cost of reduced efficiency, as the differencing has the effect of discarding information from the data.

Changing to standard regression notation, the regression discontinuity design can be written as:\(\hbox {DIV}_{\textrm{it}}\) represents the dividends of firm i in year t. Here the treatment effect is represented by the coefficient \(\tau \) on the indicator \(\hbox {NoAudit}_{\textrm{it}}\), whether firm i forgoes an audit in year t. \( f(\textbf{SIZE})\) represents the function of the firm size variables that determine the thresholds for the audit exemption. \(\textbf{X} \beta \) and \(\textbf{Z}\gamma \) represent vectors of observed and unobserved variables and corresponding vectors of coefficients. Examples of unobserved variables that might affect dividends include manager personality and risk appetite.

In this specification, \(\tau \) is the discontinuity at the threshold value of the policy, conditional on the control variables. The estimate of \(\tau \), \(\hat{\tau }\), is only unbiased if the selection into the treatment is not dependent on the unobserved covariates \(\textbf{Z}\): \(E(\tau |\mathbf {f(SIZE), X, Z}) = E(\tau |\mathbf {f(SIZE), X})\).

Covariates are chosen so as not to control for post-treatment variables, which will tend to bias the estimated coefficients toward zero (Gelman and Hill 2006). Controlling for earnings and cash flow as well as other flow variables in the financial accounts could then partially control for the effect on dividends that we wish to estimate. On the other hand, variables like earnings and cash flow also have a straightforward relationship to dividends as these are determinants of a firm’s ability to pay dividends in the first place. We include control variables for firm size: Operating revenue, total assets, and number of employees. Stock variables, like leverage, reflecting a history of the firm’s activities, are also included. Flow variables, like cash-flow, that fully reflect year-to-year variation are not included. Instead, we include firm average and standard deviation of cash-flow over the years 2005–2015. We also include the 1-year lag of operating income, though this variable does not materially alter the estimation of the coefficient on the noAudit indicator. Since the variable for within-firm average cash flow already controls for the general level of profitability of a firm (cash flow is defined as operating income plus depreciation), we omit the lagged operating income variable following the first set of discontinuity regressions.

The main empirical challenge in this article is that the correct control group—firms that were not eligible to forgo an auditor but would have forgone an auditor if they had the opportunity—is not observed. In the previous section, we have attempted to correct for this potential source of bias by including linear control variables in our estimation. We have also introduced a nonparametric representation of the forcing variable—operating revenue—to take account of the potential for a nonlinear relationship with dividend policy. Still, such controls only partially correct for imbalance between treatment and control groups (Imbens and Rubin 2015).

In this section, we attempt to directly improve the balance between the treatment and control groups using propensity score matching (Rubin 1979; Imbens and Rubin 2015). Intuitively, we are seeking to create an artificial control group that most resembles the treatment group.

We start by creating a logit regression model with all firms that were eligible to forgo an audit, where the dependent variable is whether they chose to forgo auditing (1) or not (0). This can be represented simply as in Eq. 7, where \(\textbf{X}\) represents the matrix of predictor terms. The predicted log-odds from this model, \(\hbox {logit}(\hat{Y_{\textrm{noaudit}}})\), which we will refer to as \(\hat{l}\), are the propensity scores.In the matrix of predictors for the propensity score model, we include the continuous variables operating revenue, employees, total assets, leverage, return on assets and the mean and standard deviation of cash flow. We also include squared terms for all these variables as well as interaction effects between employees and operating revenue. We include fixed effects for years and industry sector. The model is complex, but the main purpose is not descriptive or interpretive, but rather to create the best possible balance between treatment and control.

From the logit model, we create the propensity scores for the treatment group, \(\hat{l}_{\textrm{treat}}\), consisting of the observations with firms under the threshold who chose to forgo auditing. A histogram of the treatment propensity scores is shown in the top panel of Fig. 9. We also create propensity scores for the sample of potential controls—firms not eligible to forgo auditing—that we can designate \(\hat{l}_{\textrm{unmatched}}\). A histogram of these propensity scores is shown in the middle panel of Fig. 9. The figure shows that the treatment and unmatched control groups are poorly balanced. We then use a nearest-neighbor matching algorithm so that for each treatment observation, a control observation with propensity score, \(\hat{l}_{\textrm{con}}\), is chosen such that the squared difference, \((\hat{l}_{\textrm{treat}}-\hat{l}_{\textrm{con}})^2\), is minimized. A histogram of the matched control sample is shown in the bottom panel of Fig. 9. The balance between the treatment and control is now improved.

With a balanced control, we proceed with the regression analysis. The results are presented in Table 8. In the first column, only the noAudit indicator- and year-fixed effects are included in the regression. This regression can be seen as a simple comparison of means in the treatment and control groups. The coefficient on the noAudit indicator is estimated to be positive and significant. In the second column, we add operating revenue as a control variable. We can now interpret the treatment indicator at the policy threshold for operating revenue, rather than just comparing means between groups. The estimated coefficient on the treatment indicator is now nearly doubled to 0.109 standard deviations. In the third column, we also add the other continuous variables as controls, and in the fourth column, we add sector-fixed effects. In the fifth column, we limit the sample to firms with operating revenue within one million NOK of the threshold. The estimated coefficient on the treatment indicator, noAudit, remains in the range of 0.10–0.16 standard deviations. Converted back to the original units, this corresponds to between approximately 40,000 and 60,000 NOK (€4000–6000).

The regression discontinuity design takes advantage of the arbitrariness of the policy thresholds on firm size. However, the design does not make full use of the panel of data to inform the estimates, as only data after the introduction of the policy is used.

As a robustness check, we make use of data prior to the introduction of the policy to do a difference-in-difference estimation. The basic intuition is that by comparing not just between treatment and control groups but also before and after the introduction of the policy, the effect of unobserved time-invariant covariates that affects selection into the treatment group can be controlled for.

The level of dividends is a key decision that managers of small private firms make. Dividends reward owners for the capital they have invested. In the case of small firms where owners often serve as managers, dividends also reward the large expenditures of time and effort that owners often put into their firms. Yet managers and owners of small firms may lack financial and accounting sophistication and may not be fully aware of conservative accounting principles.

Auditing can have the effect of promoting the consistent application of conservative accounting principles and imposing a degree of financial discipline. All else equals, this will have the effect of reducing current earnings and in turn constraining dividends.

Our hypothesis is that forgoing an audit following the implementation of an audit exemption policy for small firms in Norway could lead to an increase in dividends, all else equal. Using a regression discontinuity design with both linear and nonparametric representations of the forcing variable, propensity score matching as well as difference-in-difference estimation, we consistently find statistically and economically significant effects of forgoing an audit. A representative firm on the eligibility threshold that could, and did forgo an audit, increased their average dividend by between 35 and 85,000 NOK (€4000–€9000) compared to similar firms just above the threshold. This amount is greater than the average cost savings of forgoing an audit.

The results presented in this paper have limitations. For one, the regression discontinuity design requires that results be interpreted at the discontinuity threshold. Extrapolating the results both toward much smaller or much larger firms is not necessarily directly supported by the analysis. On the other hand, we have ex ante no reason to believe that the results should hold only at the threshold. The theoretical underpinnings for our analysis are not contingent on a particular firm size. Neither is there anything in our empirical study that would indicate that the findings are limited to firms of a certain size.

The results should not be extrapolated to the extremes of either very small, owner-employee firms or large publicly listed firms. Yet even if the results pertain primarily to small- and medium-sized firms, the results are nonetheless important. Small- and medium-sized firms make up sizeable portions of employment and turnover in most developed economies yet receive relatively little attention by researchers compared to large publicly traded firms. The results also contribute to the understanding of auditor exemption policies. Our results indicate that the implementation of the exemption policy in Norway lead to a change in real economic behavior among small firms who did not obtain an audit. Our research does not support a normative interpretation of this change in behavior, and however, we consider a judgment of the optimality of the audit exemption policy or any level of dividends as outside the scope of this article. This article also provides evidence supporting the role of auditors in promoting accounting conservatism, and in turn how accounting conservatism can have real economic effects on the behavior of small firms.