Abstract
I test whether information spillover concerns are a causal determinant of supplier choice and whether suppliers are a conduit for these spillovers. Using the audit setting, where firms must use the services of an auditor to certify their financial statements, I document a reluctance of rival firms to engage the same auditor due to information-spillover concerns. This reluctance mitigates the benefits of industry specialization by auditors shown in prior literature. Using several quasi-natural experiments that exogenously vary the information-spillover costs of sharing the same auditor, while keeping the benefits of industry specialization constant, I find that same-industry rivals become less (more) likely to share the same auditor when the costs of information spillovers increase (decrease). I also find that firms initially sharing the same auditor make less similar decisions following an exogenous shock that compels them to switch auditors, suggesting that a legitimate reason may exist for client concerns about information spillovers.
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Notes
Ernst & Young appears to have resigned upon Coca-Cola’s request (Cowan 1990).
Demski et al. consider client information leakage across divisions of a professional firm and incentive mechanisms for efficiently dealing with such spillovers. Hughes and Kao consider the alternative of a vertically integrated firm, facing downstream competition, to spin off an upstream supplier to preclude transmission of rivals’ proprietary information and preserve upstream sales to those rivals. Dye and Sridhar consider the firm’s choice to consult outsiders to acquire additional information about a new project, when doing so exposes the firm to information leakage. In Baccara’s model, a firm chooses between outsourcing production, thereby exposing it to leakage to competitors, and in-house production, which comes with the loss of some efficiency. Bönte and Wiethaus consider a choice between increasing the efficiency of a supplier by providing technical knowledge and risking transmission of that knowledge to competitors serviced by the same supplier.
Some auditor mergers may not have taken place because the audit firms feared that same-industry clients might leave after the merger. An analysis of auditor-merger rumors in Factiva indicates that several mergers considered by the Big Eight auditors did not happen. However, this concern goes against finding the results. In particular, my results indicate that, for the mergers that took place, same-industry rivals were still more likely to switch auditors when faced with the prospect of having their auditor covering a rival. This suggests that the reluctance of same-industry rivals to share the same auditor is higher than what is documented from the merger test.
Noncompete agreements, with an enforcement level that depends on the state where the employee works, are highly effective at restricting employee mobility across rivals (e.g., Garmaise 2011; Marx et al. 2009). Aobdia (2014) finds that a higher enforcement level of noncompete agreements is associated with less voluntary disclosure to the capital markets, consistent with a lack of enforcement of noncompete agreements reducing the proprietary costs of disclosure because of increased employee mobility across rivals.
The social networks literature finds that executives are strongly influenced by social interactions. Prior literature finds that Harvard MBA executives from the same cohort make more similar decisions for their firms, especially following alumni reunions (Shue 2013). This result suggests that alumni attending these reunions transmit information that has an impact on firms’ decisions. Similarly, the auditor is part of a network, and two firms sharing the same auditor may be connected through the personnel from the shared auditing firm.
This analysis alleviates selection-bias concerns, present in association-based studies, whereby more similar firms choose the same auditor. In a prior version of this paper, I found, in association-based tests, that firms sharing the same auditor have closer decisions than firms not sharing the same auditor. These results persist after enactment of the 2002 Sarbanes–Oxley Act (SOX), which prevented auditors from cross-selling many types of consulting services to their auditing clients, suggesting that the core auditing practice is a conduit for information spillovers.
Kwon (1996) attempts to test this hypothesis. However, the dependent variables in the study, the average number of clients per auditor for each industry and a measure of dispersion of this number, are both proportional to the number of clients in the industry when the number of auditors is limited. Consequently, the documented negative association with industry concentration appears to be mechanical and could still be found when assuming the null of random allocation of client firms to auditors. Simulation results are available from the author upon request. Cahan et al. (2008) also incorporate in some of their tests the reluctance of same-industry rivals to share the same auditor but use similar dependent variables as in Kwon (1996). Dunn and Mayhew (2004) and Dunn (2011) also mention this hypothesis as a tension going against their results but do not formally test it.
Grant Thornton, which was called Alexander Grant & Company at the time, was sued by Consolidata and lost. This precedent provides powerful incentives for auditors to hide any potential information leakage from one client to another for reputation and litigation purposes. Werner (2009) also reports that Grant Thornton raised concerns about the collectability of accounts receivable at one client because it had learned that the buyer, another client, would be unable to pay for the goods purchased. Additional examples of information leakage can also be found within the consulting arms of Big N audit firms (e.g., Raice and Rapoport 2013; O’Shea and Madigan 1998).
Both examples are related to insider trading, an activity easier to uncover than information leakage from one client to another, given a higher level of monitoring by the financial authorities. These examples also confirm that auditors have access to important client information. Examples of information spillovers from one client to another available in the public domain have been difficult to find since the Consolidata case.
Best practices may represent an institutionalized channel for information spillovers in auditing, because general knowledge and expertise obtained through a client engagement are not considered confidential information (e.g., Cashell and Fuerman 1995). This leaves the door open for auditors to disseminate knowledge through the form of best practices. Anecdotal evidence indicates that this mechanism appears to be employed.
Prior research often established information-spillover links using patent citations, following Jaffe et al. (1993). However, several papers show that the information transmitted by employees goes beyond purely technical information. For example, Boeker (1997) and Rao and Drazin (2002) find that firms hiring managers from their rivals have subsequently entered some of the product markets of their rivals.
Garmaise (2011) reports that 70 % of firms have noncompete agreements with their top executives and that their enforcement reduces within-industry transfers of executives by almost 50 %. The Society for Human Resource Management, in a survey conducted in 2007, found that 56 % of organizations require employees to sign noncompete agreements. Marx (2011) finds that technical workers subject to a noncompete agreement are 88 % more likely to switch industries when changing jobs, compared with 28 % of workers not subject to a noncompete agreement.
This literature finds causal evidence that more connected executives make more similar decisions, consistent with information being transferred through social networks. Similarly, the auditor can be assumed to be part of a social network with its clients.
I kept companies headquartered in tax havens as per the OECD definition (GAO 2008), because these firms are often U.S. firms expatriated abroad for tax reasons (see, for example, Desai 2002). The merger analysis, by design, focuses on top-tier auditors. Other analyses focus on firms initially covered by top-tier auditors (Big Eight to Big Four, depending on the period) to limit the impact of other variables influencing auditor choice.
Using NAICS codes at the six-digit level has several advantages over other product-market classifications. The classification is up to date, in contrast to the four-digit SIC codes, and is more granular than the SIC, GIC, and Hoberg and Phillips (2010) classifications. The historical data also spans a longer period than the other classifications, a critical advantage for incorporating as many natural experiments as possible in the analysis.
Asker and Ljungqvist (2010) present a similar test of bank mergers in the context of securities underwriting.
Ernst & Whinney merged with Arthur Young in October 1989, Deloitte, Haskins and Sells merged with Touche Ross in December 1989, and Price Waterhouse merged with Coopers Lybrand in July 1998.
I confirmed that there was no ruling by the Department of Justice or Federal Trade Commission that compelled the newly merged auditor to divest some of its clients due to a dominant position of the merged auditor in specific industries. Such a ruling could have biased the specifications toward my results.
I initially focus on the top-three players in each industry to increase the power of the tests. Larger firms within each industry are more likely to be true product-market rivals. In addition, because of the limited number of auditors, only large firms have the option to switch to another auditor who is not covering large rivals. Smaller firms may not have this opportunity, especially in industries with multiple players. A caveat of this analysis is that it may not be generalizable to all firms in an industry.
Untabulated results confirm that firms covered by merging auditors switched auditors more than firms not covered by merging auditors. This proportion is 10 % (31 %) higher for the top-three (top-ten) firms in each industry.
All continuous variables are winsorized at the 1 and 99 % levels to reduce the impact of outliers.
See “Appendix 1” for additional details on the variables.
Results could also be consistent with industry rivals not wanting to share the same auditor due to the appearance of collusion or to avoid having to align their accounting with each other. If these alternative explanations were valid, predictions would be similar to the supply-based explanation described in the text.
The tariff results presented in Section 3.3 could be subject to an alternative interpretation whereby, because of increased pressure on the margins of the firms impacted by the tariff shocks, these firms would renegotiate their supplier contracts, including with their auditors. This could lead to the impacted firms switching auditors more often. In untabulated tests, I confirm that the profit margin and gross profit margin of the impacted firms decline in comparison with the control group of non-impacted firms. However, I do not find evidence of increased auditor-switching activity following the tariff shock. In addition, because audit fees increase approximately with the square root of the clients’ assets (e.g., Simunic 1980), increased switching should be expected for smaller firms impacted by the tariff shocks, because audit fees represent a higher burden for smaller firms than for larger firms. I partition the sample between smaller and larger firms but still do not find evidence of increased auditor switching following the tariff shock, even for the smaller firms. Overall, these results suggest that the results presented in Sect. 3.3 are more consistent with information spillovers than with an overall supplier renegotiation story, even though it is impossible to rule out this alternative explanation.
The data are available at http://faculty.som.yale.edu/peterschott/sub_international.htm.
Results are robust when I include all tariff cuts within given industries with the restriction, for data-construction purposes in the difference in differences test, that the tariff cuts be at least 4 years apart within the same industry. Results are also robust to different assumptions on tariff reductions—for example, when a large tariff cut is defined as 1 % or more.
I keep the observations only when the data are available for both before and after the tariff shock, and I create only one pair for the combinations i,j and j,i.
Because of the large number of fixed effects used in Columns (3) and (4), I replace the logistic regression with OLS. Clustering standard errors at the industry level in Column (4) alleviates concerns of inflated t-statistics coming from the multiplication of paired observations, because each pair of firms belongs to the same industry.
This number is computed as −0.02, corresponding to the coefficient on Impacted Industry × After Impact, divided by the average propensity for a pair of firms to share the same auditor, or Sameauditor, equal to 0.19.
One may wonder whether the Private Securities Litigation Reform Act of 1995 (PSLRA) may have an impact on the results, given that auditors’ liability went down, especially in higher risk industries, following the implementation of the act (e.g., Lee and Mande 2003). This may have led to a supply shock whereby auditors are more willing to take clients within the same industry. I conduct a robustness test by eliminating high litigation industries (computer, electronics, pharmaceutical/biotechnology, and retailing, as in Ali and Kallapur 2001) from the sample around 1995, and I find stronger results.
In contrast to Garmaise (2011), I cannot use the change in the enforcement of noncompete agreements for the states of Florida and Louisiana, because both happened at the time of the potentially confounding events of auditor mergers and the collapse of Arthur Andersen. In addition, changes in Florida were not as drastic as in Texas, and changes in Louisiana were temporary, lasting only two years.
The Noncompete State variable is set equal to zero for the state of Texas, as the difference-in-differences specification already takes into account the change of this variable. Consequently, results on the Noncompete State are valid for the remaining states in this analysis.
Given that auditor–client relationships are reasonably sticky over time, one may wonder how the results would change when looking at years 1996 and 1997 instead of 1995 in model (2). In particular, if information spillovers increase over time as employee mobility increases, industry rivals would progressively become more likely to share the same auditor over time. Untabulated analyses indicate that the results become progressively stronger when looking at years 1996 and 1997 instead of 1995, consistent with this hypothesis.
Because I include year fixed effects in the analysis and only two years are considered, the After Impact variable is not identified, in contrast to Table 4.
This number is equal to the coefficient on Texas × After Impact (0.01), divided by the sample average of Sameauditor (0.22).
This value is equal to the coefficient on Noncompete State (0.05) divided by the sample average of Sameauditor (0.22).
The analysis is also similar in spirit to the pair model of De Franco et al. (2011).
Similar to Dyreng et al. (2010), I set as missing effective tax rates (ETRs) with negative pretax income and winsorize nonmissing ETRs so that the largest observation is one and the smallest is zero. In addition, missing SG&A, R&D, advertising, and investment variables are set equal to zero when used as independent variables in model (5). To avoid potential bias in the computation of the residuals in models (3) and (4), I exclude observations with missing values when no company in the same industry has a positive value for the variable.
Data are obtained from Compustat. I keep firms covered by Big N auditors, for which data on investment and first-stage regression control variables are available, and eliminate subsidiaries. The MSA data are from the U.S. Census Bureau and are matched using the zip code. This restricts the sample to firms headquartered in the U.S. The final sample for the first-stage regression contains 91,900 firm years, spanning from 1985 to 2011. The results of the first-stage regressions are untabulated and available upon request.
I do not control in the reported specifications for whether the pair of firms formerly covered by Arthur Andersen switched to the same auditor or a different one, because all potential channels for information spillovers, including formal and informal communications channels among colleagues, are likely to have been broken regardless of the next auditor choice, and it may take some time to build new ones. For example, even if the client followed its former auditor (Kohlbeck et al. 2008), anecdotal evidence suggests that the former Arthur Andersen employees, assuming they actually went to work for the acquiring auditor, moved to different offices (e.g., Goelzer 2004), thereby breaking some informal channels of information transfer. Furthermore, team staffing is likely to have changed to better integrate former Arthur Andersen teams with the acquiring auditor. Untabulated tests indicate that there is no major difference in terms of divergence of decisions for pairs of firms initially covered by Andersen that switched to the same auditor or to a different auditor, consistent with the initial channels for information spillovers being broken regardless of the next auditor choice.
Only one pair is created for the two combinations i,j and j,i.
Sameindustry controls for potential selection bias for same-industry rivals. Results are qualitatively similar when excluding same-industry pairs from the specifications.
I use a design similar to that of Shue (2013) to compute the statistical significance of the regression coefficients, based on Monte Carlo simulation. The purpose is to control for any potential time and firm dependence across pair-years that could impact the independence of the standard errors and inflate the t-statistics. A potential concern of the pair analysis is that the decision of each firm appears in multiple pair observations. In addition, for a given pair of firms, the difference in decisions may be correlated over time. To take care of this, I adopt a design similar to Shue’s (2013), whereby, for each regression, I conduct a Monte Carlo simulation of placebo effects to determine a null distribution of the βs. Specifically, for each regression, I simulate 1000 placebo specifications in which I randomly assign the explanatory variables to randomly chosen pairs of firms. The assignments are kept similar for 2001 and 2003 for each pair of firms within a given placebo specification, to control for potential correlation over time. I then compare the actual value of the βs to their null distribution to compute a nonparametric p value. In untabulated tests, I also re-run the specifications by clustering standard errors at the pair level and find stronger results.
The tenor of the results is unchanged when the interaction Samemsa × Andersenfirm × Y2003 is replaced with Sameoffice × Andersenfirm × 2003, where Sameoffice is computed using exact Arthur Andersen office-client coverage information from Audit Analytics, instead of a proxy for when firms are headquartered in the same MSA.
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Acknowledgments
This paper is based on my dissertation at the UCLA Anderson School of Management, originally titled “Proprietary Information Spillovers and Auditor Choice.” I am highly indebted to my dissertation committee members—David Aboody, Judson Caskey, Hugo Hopenhayn, Jack Hughes (chair), and Brett Trueman —for their invaluable guidance and support. I also thank Stephen Penman (editor), two anonymous referees, Ray Ball, Randolph Beatty, Craig Chapman, Jon Lewellen, Thomas Lys, Robert Magee, Mariko Sakakibara, Richard Sansing, Junko Sasaki, Beverly Walther, and seminar participants at Columbia University, Dartmouth College, INSEAD, London Business School, Massachusetts Institute of Technology, Northwestern University, New York University, Stanford University, UCLA Anderson School of Management, University of Chicago, University of Michigan, University of Utah, and Wharton School of the University of Pennsylvania for their helpful comments and discussions on previous versions of this paper. I also thank Laurent Fresard for helpful comments on the import data and Peter Schott for making the import data available on his website. I gratefully acknowledge financial support from the Deloitte Foundation. I wrote this paper before joining the Public Company Accounting Oversight Board (PCAOB). The views expressed in this paper are my own and do not necessarily reflect the views of the Board, individual Board members, or staff of the PCAOB.
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Aobdia, D. Proprietary information spillovers and supplier choice: evidence from auditors. Rev Account Stud 20, 1504–1539 (2015). https://doi.org/10.1007/s11142-015-9327-x
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DOI: https://doi.org/10.1007/s11142-015-9327-x