Fraudulent Financial Reporting

and the Consequences for Employees

Jung Ho Choi

Brandon Gipper

Stanford University

Graduate School of Business

July 2018

-Preliminary and Incomplete-

Please do not cite or circulate.

Note on the presentation of our results

In this paper, we present preliminary results from our analyses. Specifically, we give “qualitative”

output from tests of differences and regression estimates. Qualitative output includes signs of

differences in averages and signs of coefficient estimates along with significance at conventional

levels. We do not present numerical descriptive statistics, magnitudes of coefficient estimates,

observation count, nor model fit. The reason for this presentation choice is that we have two

options for making publicly available our results when using U.S. Census data, (i) this qualitative

output or (ii) typical, quantitative output. We face a significant constraint in presenting typical,

quantitative output. If our sample changes slightly (e.g., from a change in research design), then

we may not be able to present any new results because these small sample changes are not

acceptable to the U.S. Census Bureau for public disclosure. This constraint is made tighter by use

of AAER data: we identify 593 accounting-fraud firms (with affected annual financial statements)

matched to Compustat data in the U.S. from 1982 to 2014 (but before matching to U.S. Census

data). This relatively small set of AAERs makes unacceptable sample changes more likely with

design changes. We thought it best to seek feedback on our research design choices and structure

of analyses using qualitative output so that we can have flexibility to have small sample changes

and be able to make new results publicly available as typical, quantitative output in future versions

of this paper.

Fraudulent Financial Reporting

and the Consequences for Employees*

Jung Ho Choi

Brandon Gipper

Stanford University

Graduate School of Business

July 2018

-Preliminary and Incomplete-

Please do not cite or circulate.

Abstract

We examine employment effects, such as wages and employee turnover, before, during, and after

periods of fraudulent financial reporting. To analyze these effects, we combine U.S. Census data

with SEC enforcement actions against firms with serious misreporting (“fraud”). We find that

compared to a matched sample, employee wages decline during and after fraud, although

employment growth at fraud firms is positive before and during fraud periods and negative after.

We discuss several channels that plausibly drive these findings. During fraud, managers overinvest

in labor. Frauds cause informational opacity, and fraudulent reports tend to indicate good

prospects, encouraging employees to still join the firm or to continue to work at lower wages in

anticipation of future wage growth. After the fraud is revealed and the overemployment is

unwound, employee wages will fall due to turnover, with related job-search challenges and losses

of firm-specific investments, and the stigma associated with the fraud. We use various subsamples

to provide evidence for these mechanisms, showing that fraudulent financial reporting appears to

be related to informational frictions and that labor market disruptions and stigma have meaningful

and negative consequences for employees.

JEL classification: D83, J23, J31, M48, M51

Key Words: Wages, Employment Growth, Accounting Fraud, Information Asymmetry,

Stigma

* Contact: jungho@stanford.edu and gipperbr@stanford.edu. Any opinions and conclusions expressed herein are

those of the authors and do not necessarily represent the views of the U.S. Census Bureau. All results have been

reviewed to ensure that no confidential information is disclosed. We thank Ray Ball, Phil Berger, Nick Bloom,

Hans Christensen, Steve Davis, Sheffield E Lesure, Christian Leuz, Frank Limehouse, and Sorabh Tomar. This

research uses data from the Census Bureau's Longitudinal Employer Household Dynamics Program, which was

partially supported by the following National Science Foundation Grants SES-9978093, SES-0339191 and ITR-

0427889; National Institute on Aging Grant AG018854; and grants from the Alfred P. Sloan Foundation. We thank

Stanford University for funding and the Centers and Initiatives for Research, Curriculum & Learning Experiences

for research assistance.

1

1. Introduction

In this paper, we examine the consequences for employees from fraudulent financial reporting

(also “accounting fraud” or “misreporting”),1 and we find them to be dynamic and significant.

Employees are important stakeholders of the firm; their long-run fortunes rise and fall with those

of firms through, for example, investment in firm-specific capital (Becker, 1993) or risk-sharing

(Baily, 1974). Prior papers have looked at the consequences for employees from economic shocks,

such as regulation, offshoring, or bankruptcy (e.g., Walker, 2013; Hummels, Jorgensen, Munch,

and Xiang, 2014; Graham, Kim, Li, and Qiu, 2016). Accounting fraud has two features often

distinct from these other shocks. First, it is discretionary; presumably, executives could choose to

properly report financial performance. Second, executives attempt to hide accounting fraud;

employees could suffer (or benefit) for reasons that are opaque. These features suggest

misreporting can be relevant for employees but unknown to them and avoided with sufficient

governance mechanisms, at the firm or as regulation. Therefore, documenting the consequences

for employees, who are often incidental to the accounting fraud—unlike executives (e.g., Desai,

Hogan, and Wilkins, 2006; Karpoff, Lee, and Martin, 2008a)—but may suffer nonetheless is

important. We ask and answer several empirical questions: Do employees suffer financially prior

to revelation or benefit from misreporting in the form of higher wages, and does this effect vary

by period of hire? After revelation, do they suffer from wage declines or turnover? If we observe

such effects, why?

1 Schrand and Zechman (2012) make a distinction between “fraud” and “misreporting” from pleading standards in

10b-5 actions; that is, for “fraud,” the executives met or were likely to meet some notion of intent or scienter. For

instance, the executives had motives evidenced by explicit personal gain. “Misreporting” does not meet such a

standard. We do not make the distinction here, because we are not examining executive motives, other executive

behaviors, or consequences for executives. We use these terms interchangeably.

2

Two empirical challenges arise from these research questions. First, employee data are not

commonly available. We use the Longitudinal Employer Household Dynamics and Longitudinal

Business Database datasets from the U.S. Census Bureau, an increasingly important data source

for addressing questions related to employees in the United States (e.g., Hyatt and McEntarfer,

2012). We match this employer-employee data with Accounting and Auditing Enforcement

Release (AAER) data to proxy for fraudulent financial reporting. Our final sample includes cases

of misreporting from firms employing a worker in one of 23 states2 over the period 1991–2008.

Second, firms could be simultaneously experiencing economic shocks that cannot easily be

disentangled from the effects of the fraud. When executives commit accounting fraud, they tend

to be covering up minor shocks or excessive optimism; that is, they are on the “slippery slope”

(Schrand and Zechman, 2012). For our main tests, we use propensity-score-matched firms within

industry and year. We also perform robustness tests to vary our control sample, including random

employees at unmatched firms within industry.3 These data and matching method provide a

reasonably comprehensive and powerful sample to address our research questions.

We find that employees at fraud firms, compared to a matched sample, have lower earnings

on average during and after periods of fraudulent financial reporting. This result is robust to a

variety of specifications—including models with extensive effects to rule out other shocks such as

regional, industry downturns—and control groups. Sample splits by period of hire show that

existing employees (those at the firm prior to the misreporting) have negative earnings trends

2 The application process for using U.S. Census data for academic studies requires that individual states approve the

project’s use of data from that state. For an AAER case to enter our sample, the misreporting firm must have an

employee with unemployment insurance in a participating state, among our other sample criteria. 3 We caution that matching does not fully resolve endogeneity issues (e.g., Roberts and Whited, 2013). However,

descriptive data still provide highly useful evidence toward the understanding of more general effects of fraudulent

financial reporting. We also note that some consequences for employees can be indirect effects from other real

actions taken by executives during periods of misreporting. For instance, executives could overinvest in capital

(McNichols and Stubben, 2008) and affect wages for employees who manage this new capital stock.

3

during and after the fraud. New employees (those hired into the firm in the first year of

misreporting) only suffer negative earnings trends in the post-fraud period. Thus, fraudulent

financial reporting seems to disproportionately affect long-tenured employees. These wage

declines exist despite increased employment growth at fraud firms before and during the

accounting fraud. We see negative employment growth at fraud firms after the fraud concludes.4

Displaced workers are more likely to leave the industry and even the county, taking their next job

(if any) elsewhere. Descriptive splits show that worker displacement contributes substantially to

the average wage effects at fraud firms.

We show evidence consistent with several channels for these wage effects. First, managers

overinvest in labor in the fraud period (Kedia and Philippon, 2009). We argue that if workers are

aware of accounting fraud, then they require wage premiums for risk-sharing with these

informationally opaque firms. So, this upward shift in labor supply combined with an outward shift

in labor demand would cause wages to rise during fraud periods. Instead, the absence of an increase

in wages for new and existing employees combined with employment growth at fraud firms

indicates that workers do not identify the accounting fraud, and thus they do not price protect

against it. Workers, like shareholders, suffer from firm-specific information asymmetry when

executives perpetrate fraudulent financial reporting.

Second, we analyze a subsample of fraud- and control-firm employees who leave, and we find

that those leaving fraud firms earn less in the post-fraud period. Negative employment growth in

the post-fraud period follows overemployment in the fraud period. The earnings drop in the post-

fraud period is consistent with several stories: (1) workers are shocked by the fallout from the fraud

and have lost firm-/industry-specific human capital, conducted job-search activities ineffectively,

4 This result is consistent with evidence from Kedia and Philippon (2009) using employee levels from Compustat.

4

and/or entered crowded labor markets (e.g., Jacobson et al., 1993); (2) workers suffer from the

stigma associated with the fraud (e.g., Gibbons and Katz, 1991; Groysberg, Lin, and Serafeim,

2017); and (3) workers are complicit so are punished; labor markets “settle up” (Fama, 1980). We

examine two subsamples in an attempt to isolate some of these channels. Early-leaving workers,

who are less likely to face job-search complications from fraud revelation, still experience declines

in wages in the post-fraud period. Workers in the bottom 90% of the pre-fraud wage distribution

(assumed not to be complicit executives) experience, if anything, more negative wage effects

during and after fraudulent financial reporting than the top 10% of employees. The results from

these subsamples indicate the fraud-related stigma plays some role in these negative wage effects.

Finally, we analyze the relation between wage premiums and accounting quality. We find

weak, preliminary evidence that workers demand wage premiums when accounting quality is low.

This finding is consistent with workers demanding pay to compensate for a risk of labor market

disruptions due to accounting fraud. Despite this evidence, we find that existing employees have

negative wage trends in the post-fraud period, while we limit the sample to fraud- and control-firm

employees who stay at their firms. Moreover, workers at fraud firms cannot successfully demand

wage premiums for revealed, low-quality accounting. This result could indicate that job-switch

frictions prevent workers from demanding these higher wages despite revelations about the fraud

firm’s riskiness (e.g., Baily, 1974; Guiso, Pistaferri, and Schivardi, 2005; Manning, 2011).

We make several important contributions. First, our paper contributes to an extensive

literature documenting consequences for employees from a wide variety of shocks to firms. For

example, Gibbons and Katz, (1991), Jacobson, LaLonde, and Sullivan (1993), and Couch and

Placzek (2010) examine the costs to employees of mass layoffs, and they find meaningful wage

losses. Walker (2013) shows that some environmental regulations can reduce affected workers’

5

wages. Autor, Dorn, Hanson, and Song (2014) and Hummels et al. (2014) examine employee

responses to globalization and offshoring. They find that more-exposed workers received lower

earnings. Graham et al. (2016) find employees at firms that are at risk of (go through) bankruptcy

experience earnings gains (losses), driven by the lower ability to share risks by (increased

likelihood to leave) the firm. Samaniego de la Parra (2018) shows that government enforcing

regulation against informal (“off the books”) hiring has spillover effects on employees and their

spouses for subsequent labor market transitions and wages. Across these many shocks, the

consequences for employees are significant in terms of wages and worker flows. We show

complementary evidence for fraudulent financial reporting in qualitative results. During the fraud,

the informational opacity of the misreporting leads workers to not see wages go up. After the

accounting fraud is revealed, employees who are not displaced see wages drop, indicating labor

market frictions prevent workers from price-protecting themselves. However, we also observe

meaningful worker outflows; displaced employees have negative wage effects, plausibly a result

of the stigma associated with the fraud (e.g., Groysberg et al., 2017) among other reasons.

Second, we contribute to another extensive literature documenting other consequences of

fraudulent financial reporting. Some papers show specific actions taken by firms because of the

misreporting. For instance, Erickson, Hanlon, and Maydew (2004) show that firms incur real cash

outflows, namely, overpay taxes, to perpetuate fraud. McNichols and Stubben (2008) show that

firms overinvest. Other papers document broader cost estimates; Karpoff et al. (2008b) (Dyck,

Morse, and Zingales (2013)) find that firms lose about 29% (22%) of equity (enterprise) value.

Kedia and Philippon (2009) show some effects similar to ours with aggregated employee count

6

and GAO restatement data.5 Our findings are highly complementary to these prior papers by

expanding on the dynamics of employment and associated wages; we show significant worker

outflows afterward and wage effects that decline during and after the fraud. These findings are

consistent with highly disruptive and costly misreporting, even trickling down to employees. An

important subset of this literature documents consequences for executives and directors for

fraudulent financial reporting (e.g., Srinivasan, 2005; Desai et al., 2006; Karpoff et al., 2008a;

Groysberg et al., 2017). We contribute to this literature by documenting that lower-level

employees suffer consequences similar to those at the top after the fraud is revealed, for example,

higher incidence of job exits and reputational/stigma effects. This benchmark is important because

often low-level employees are not party to the fraud, whereas executives (directors) perpetrate (fail

at their monitoring duties to uncover) the misreporting, so one might expect consequences for the

latter to be more severe.

Third, our paper also contributes to an important policy debate. Regulatory reforms intended

to reduce the burdens associated with mandatory financial reporting are often politically motivated

by job creation. For instance, the Jumpstart Our Business Startups Act (JOBS Act) reduced some

disclosure and audit requirements for small and mid-sized IPO firms and was hailed by politicians

as promoting job growth (Liberto, 2012), as evidenced by the tortured name that creates its

acronym. Although we do not provide direct evidence of a regulatory regime that intends to reduce

misreporting, we show that rolling back these regimes may have nuanced effects on workers.

Reducing regulatory mechanisms (or firm-specific governance mechanisms) could be harmful to

wages and employment if executives more often engage in fraudulent financial reporting in lax,

5 Kedia and Philippon (2009) also show overinvestment, consistent with McNichols and Stubben (2008), and have

some evidence on increases in productivity after the restatement.

7

post-rollback environments. These labor market effects can be useful inputs for evidence-based

policymaking (Leuz, 2018). In addition, our findings that misreporting exacerbates labor market

frictions could be considered alongside enterprise value to measure social costs of fraudulent

financial reporting (e.g., Dyck et al., 2013).

2. Hypothesis development and institutional background

2.1. Literature Review

Prior literature has explored the causes and consequences of fraudulent financial reporting.

Executives’ private benefits and their optimism both trigger accounting fraud. Kedia and Philippon

(2009) demonstrate that executives engage in both accounting fraud and insider trading for their

private benefits. Schrand and Zechman (2012) find that an executive’s excessive optimism can

result in accounting fraud. Accounting fraud affects various parties related to these firms. Karpoff

et al. (2008b) and Dyck et al. (2013) show that accounting fraud lowers a firm’s value substantially.

McNichols and Stubben (2008) find that managers make inefficient investment decisions to hide

financial misreporting. Beatty, Liao, and Yu (2013) demonstrate that peer firms engage in

overinvestment because the inflated financial performance of fraud firms provides misleading

information about an industry’s prospects. Moreover, prior literature provides much evidence on

the relation between fraudulent financial reporting and financial markets or physical capital

markets.6

6 Prior literature also investigates the interaction between financial markets and labor markets. Davis et al. (2014)

show that target firms of private-equity buyouts experience not only small reductions in net employment, but also

an improvement in productivity. Tate and Yang (2015) find that employees in diversified firms are able to develop

human capital in the various industries in which the firms have businesses. Silva (2013) demonstrates that the wage

differentials across industries are smaller if the employees in different industries are working for the same

diversified firms. Baker (2015) shows that a financial shock to an employer affects employees differently depending

on the employees’ financial health.

8

Relative to visible costs (e.g., the cost to investors), the less visible costs of accounting fraud

(e.g., the cost to employees) are not as well documented, although this information is useful for

academics, practitioners, and regulators (Ball, 2009; Dyck et al., 2013; Leuz, 2018). This study

will examine the impact of fraudulent financial-reporting decisions on labor markets. We

understand little about the importance of executives’ financial-reporting decisions in labor

markets, particularly misreporting (except in the top executive markets, e.g., Desai et al., 2006).

However, workers are major stakeholders of the firm so could be major stakeholders in the

consequences of accounting fraud.

We predict that effects from fraud can be dynamic over the misreporting’s life cycle. We treat

the misreporting as having three distinct periods (for more about measurement, see section 3): (i)

“pre-fraud” is the four-year period prior to the beginning of the fraudulent misreporting; (ii)

“fraud” is the period of time that mandatory financial information has been seriously misreported,

later drawing SEC scrutiny, normalized to a maximum of three years; and (iii) “post-fraud” is the

six-year period after the fraud is terminated, either through manager discontinuation, revelation,

and/or firm failure.7 Although many accounting frauds are likely to be much more complex than a

simple three-period event, we believe this categorization has several advantages. First, a common

baseline in the pre-fraud period will help us select a plausible control sample to map out effects of

the accounting fraud over later periods. Second, we are able to use the effects across multiple

periods and subsamples to isolate specific economic mechanisms. Third, this research design is

consistent with prior papers that examine firm actions during and after misreporting events (e.g.,

7 We choose the length of these time periods to be consistent with prior literature (McNichols and Stubben, 2008;

Graham et al., 2016).

9

McNichols and Stubben, 2008; Kedia and Philippon, 2009).8 For most analyses, we separate

existing employees and new employees and use these groups to descriptively measure more (or

less) affected employee groups, and we show evidence consistent with distinctive economic

channels. See Figure 1.

We predict that in addition to being dynamic, fraudulent financial reporting can affect both

labor supply and demand. In particular, we discuss our predictions generically in a setting of an

individual employer facing upward-sloping supply. These settings exist when workers have firm-

specific capital (Becker, 1993; Jovanovic, 1979b). More general forms of human capital, such as

industry specific or task based (e.g., Neal, 1995; Gathmann and Schonberg, 2010), would not lead

to the same outcomes for workers, because the accounting fraud is firm specific. Labor market

frictions, such as costly job search, could generate these settings as well (Mortensen and Pissarides,

1999). Some of our discussion (e.g., “stigma;” see section 2.3) only considers one side of the

market but still assumes some inelasticity in both demand and supply.

2.2. Predictions for the fraud period

First, we discuss the effects for employees during the fraud period. On the supply side,

accounting fraud may lead workers to make inefficient labor choices. The worker is making an

important decision when accepting a new job; he or she could be losing firm-specific rents at an

old job (Jacobson et al., 1993), choosing to make new specific investments at the next job (Becker,

1993), and so on. The new employee plausibly chooses to work for firms involved in accounting

8 McNichols and Stubben (2008) map out separate effects for the three years leading up to the misreporting, the first

three years of misreporting (truncating later years), and the three years after misreporting. Kedia and Philippon

(2009) measure average effects (i.e., combined) for the two years leading up to the restated period, all restated

years, and the two years after the restated period. We use both strategies, disaggregated or combined, depending

on the analysis. We normalize the fraud period to three years by counting subsequent years as additional “third

years” to avoid separately identifying any fraud firms with descriptive data (i.e., long-lasting frauds) to comply

with Census Bureau requirements.

10

fraud, because (media coverage about) false financial performance suggests good prospects at the

firm. This financial misrepresentation makes specific investments or risk-sharing with the fraud

firm appear to be relatively attractive. They would plausibly choose to work elsewhere if they

knew the “true” performance of the firm or even that the executives were misreporting. Therefore,

accounting fraud could have negative effects on employees through two channels. First, firm-

specific information asymmetry could cause the employee to bear more risk than she prefers.

Second, and related, the misreporting could lead to mismatches between workers and firms. Thus,

supply may shift out but as an artifact of the misreporting. On the demand side, executives in

accounting-fraud firms appear to overinvest in capital and over-hire employees in order to bolster

the perception of the firm (Kedia and Philippon, 2009). Through both supply and demand effects,

we expect employment to grow; this finding would be consistent with results in prior literature.

Wages allow us to refine our hypothesis. On the supply side, if new workers (existing

employees) make job choices in the presence of these informational asymmetries about firm

performance, they plausibly accept normal or lower pay (pay paths) and still join (do not leave)

the misreporting firm. Indeed, fraudulent reports tend to indicate good prospects, encouraging

employees to still join the firm or to continue to work at lower wages in anticipation of future wage

growth. If wages increase during fraud, there are both supply and demand stories. For supply,

workers identify that the firm is misreporting and therefore risky, and they price protect against

the increased likelihood of suffering a negative wage shock in the future that the firm cannot insure

(Baily, 1974; Guiso et al., 2005).9 For demand, it is not a priori obvious that the firm will (or even

9 If workers believe that reporting quality is low, without identifying the accounting fraud, they may require wage

premiums to protect themselves against uncertainty about misreporting. This possibility would reduce our ability

to determine whether workers can identify and avoid or demand higher wages from fraud firms. Descriptively, we

use the full sample of public firms to test whether workers demand wage premiums for low-quality reporting. We

11

can) raise wages to attract or retain these employees.10 However, other evidence shows that

executives are willing to incur real costs to perpetuate frauds (Erickson et al., 2004). Relatedly,

managers could overinvest in labor, raising wages and the total wage bill.

2.3. Predictions for the post-fraud period

Next, we discuss the effects for employees during the post-fraud period. We first discuss

demand effects; three reasons explain why demand will contract in the post-fraud period. First,

conditional on excess hiring during the fraud period, firms will reduce this inefficient hiring when

the fraud concludes. Second, accounting fraud indicates some governance failure at the firm.

Afterward, boards or shareholders could take away decision rights from executives and undertake

projects with more caution, causing demand for labor (and other inputs) to contract (Farber, 2005;

Wilson, 2008). Third, Schrand and Zechman (2012) show that excessive optimism (covering up

small shocks) tends to precede fraud, which can unravel afterward (if the shock worsens);

naturally, demand for labor declines with a negative shock. These demand effects would cause

employment growth to be negative in the post-fraud period.11

find weak evidence that workers receive more pay when high-growth firms have higher absolute accruals,

controlling for other determinants of wages. See section 5.3. 10 McNichols and Stubben (2008) also find that firms increase R&D spending but less than capital investments. They

attribute this magnitude difference to the immediate effect of R&D expense on net income. Investing in (or hiring

/ paying more to) workers also immediately reduces net income, unless paid with options prior to expensing in

2006 (Core and Guay, 2001). However, this income-statement effect could plausibly deter executives from

excessive hiring during fraud periods. 11 We are most interested in the first and second explanations: labor force corrections and governance-induced

tightening. We are also interested in the behavioral story from Schrand and Zechman (2012) that executives can

display excessive optimism, and it can unravel. We are less interested in measuring hiring and wage responses to

negative shocks, which are straightforward and bad for workers. We include control variables and match with

employees at control firms to disentangle effects from shocks.

12

Fraudulent financial reporting can also affect peer firm demand.12 We focus on effects that

can result from a fraud firm’s reputational damage affecting employees in labor markets, that is,

“stigma.” That is, even though an employee is not obviously involved with the financial-reporting

fraud, other employers could associate that portion of the worker’s job history with the reputation

of the firm, which is damaged from the revealed fraud. This reaction of hiring managers may be

behavioral; the worker could have the same skills and productivity as other applicants but is hired

less often or paid less (Groysberg et al., 2017). Alternatively, the other employers are responding

to some probability that a worker from the now-revealed fraudulent firm is less productive or may

have been involved in the fraud (Gibbons and Katz, 1991). Disentangling these stories is

empirically challenging, though we examine subsamples of employees that earn less in the pre-

fraud period so are plausibly less likely to be the executives involved in accounting fraud. The

wage effects of stigma are straightforward; we expect former employees of fraud firms to have

lower pay, all else equal.

Next, we discuss supply effects. As discussed above, employees hired during fraud periods

plausibly decide to work for the fraud firm based on incorrect perceptions of financial

performance, which could generate less efficient worker-firm matches. Due to this information

friction influencing the match, she could have less valuable specific investments with the fraud

firm than elsewhere. And when the fraud is revealed, she loses firm-specific investments and

informational value of employer-employee match quality (e.g., Becker, 1993; Jovanovic, 1979a,

1979b). Employees could decide to search for a new job. That is, labor providers (like capital

providers, e.g., Dyck et al., 2013) take their resources elsewhere after the information asymmetries

12 For now, we sidestep spillover effects from peer firms responding to the perceived performance of fraud firms (e.g.,

Beatty et al., 2013). If our control firms or random employees at same-industry firms are well chosen, we measure

effects incremental to these spillovers. In some tests, we also report regression results from specifications with

year-industry-county effects, which control for time-varying, regional industry shocks.

13

from fraud are resolved. The result is a contraction in supply, so we expect negative employment

growth at fraud firms. Similarly, the revelation could cause a loss in reporting credibility

(Anderson and Yohn, 2002; Farber, 2005; Wilson, 2008), which would cause workers to contract

labor supply further or price protect themselves, that is, demand higher wages, because they now

have more uncertainty about the value of their match (Jovanovic, 1979a) or the ability of the firm

to share risks (Baily, 1974; Guiso et al., 2005).

Because we predict that both demand and supply contract, the effects on wages at fraud firms

in the post-fraud period are ex-ante ambiguous, though the stories for a decline in demand are

intuitively more salient. If reduced demand from fraud firms dominates, wages would decline. If

reduced supply from uncertainty over specific investments and/or match quality dominates, wages

would increase. As with our predictions for the fraud period, we measure wages to disentangle the

strength of the supply- and demand-side effects described above. Subsequent wage effects from

possible reputation damage will provide more color to the total impact on workers from accounting

fraud. We can also descriptively document total effects from the misreporting similar to Jacobson

et al. (1993) or Couch and Placzek (2010), where employees that have disruptions in their careers

could lose high wages from firm-specific capital or tenure factors. A related explanation for the

layoffs examined by Jacobson et al. (1993) is that revelation of the fraud surprises employees, so

they cannot perform a robust job search as switching workers do at control firms. Moreover, they

have conducted job-search activities ineffectively so receive lower wages if they switch jobs (e.g.,

Christensen et al., 2005; Davis, Faberman, and Haltiwanger, 2013).

14

3. Data and Research Design

3.1. Accounting and Auditing Enforcement Releases

Our sample for fraudulent financial reporting are the enforcement actions taken by the

Securities and Exchange Commission (SEC). Specifically, we use Accounting and Auditing

Enforcement Releases (AAERs). This sample identifies cases of accounting problems (among

other enforcement actions taken by the SEC) that can be connected with prosecutable, fraudulent

behavior by executives (Schrand and Zechman, 2012). We use UC Berkeley CFRM’s dataset.

Many prior papers have used these enforcement actions across a range of topics, for instance, to

estimate, describe, and measure effects of fraudulent financial reporting (e.g., Feroz, Park, and

Pastena, 1991; Beneish, 1999; Farber, 2005; Dechow, Ge, Larson, and Sloan, 2011; Groysberg et

al., 2017).

As Dechow, Ge, and Schrand (2010) point out, using the AAER sample involves a tradeoff

where Type I errors for identified misreporting are very low but sample size tends to be small and

spread out over many years. Because we are not using a particular setting that requires sharp

changes in the incidence of fraud, and because, in most analyses, we use worker-years as the unit

of analysis, increasing power, the small sample size is less costly for this study. Another tradeoff

is that SEC enforcement priorities drive AAERs. This endogenous selection criterion is more

concerning because these priorities may bias our results in a way that we cannot sign. The SEC

could pursue cases at larger firms or with larger consequences to be most effective with limited

resources. Therefore, they could pursue more impactful cases. On the other hand, the SEC could

be constrained politically and shy away from some enforcement actions (e.g., avoid “too big to

15

fail” cases). Karpoff et al. (2017) echo some of these concerns with using AAER data.13 As

mentioned above, we are not examining executive motives, other behaviors, or consequences for

executives. Our interest is in serious misreporting to measure the consequences for employees. We

believe that AAERs match the data to the research question, consistent with Karpoff et al.’s (2017)

recommendations.

3.2. U.S. Census data

We combine this AAER data with worker-firm matched data from the U.S. Census Bureau

Longitudinal Employer-Household Dynamics (LEHD) and Longitudinal Business Database

(LBD) data.

The LEHD data have a comprehensive coverage of workers, on average covering 96% of all

private-sector jobs across years (e.g., Abowd, Haltiwanger, and Lane 2004; Abowd et al., 2005).

We have data from 23 states participating in the LEHD program. These data include wage data

when the earnings are covered by a state’s unemployment insurance program and generally include

salaries, bonuses, equity, tips, and other perquisites (e.g., meals, housing, and retirement

contributions, among others) (BLS, 2016). We observe these earnings as quarterly and annual pay.

Self-employed, unemployed, and workers who move to non-participating states are not observable

in the LEHD data. The data allow us to track the wages of workers who were employed at

accounting-fraud firms but have since moved to other firms. We use this information to measure

the wage changes among job-switching employees. We also use the individual characteristics

provided by the LEHD data to separate the effects of misreporting and employee characteristics

(e.g., gender, age, education, and experience) on wages. We require that employees are between

13 Karpoff et al. (2017) indicate CFRM data perform relatively well (i.e., see their Table 8) across a variety of metrics,

except in measurement of the timing when stock market participants learn about the misreporting.

16

20 and 55 years old during the fraud period; this requirement generally limits the sample to workers

who are (or desire to be) full-time participants in the workforce. We also require that the worker’s

annual real wages are higher than $2,000 to exclude temporary workers.

The LBD data contain aggregated, establishment-level information (e.g., Davis et al., 2014;

Giroud and Mueller, 2017). It covers the universe of non-farm industries from across the United

States. The data come from the IRS and include variables such as wage bill and employment. We

use these data to track employee growth within a misreporting firm over pre-fraud, fraud, and post-

fraud periods. The LBD is also vital to merge Compustat and LEHD data. The Compustat-SSEL

Bridge (CSB) (covering 1981-2005) and the Standard Statistical Establishment List (SSEL)

(covering later years) use primarily CUSIPs to link Compustat to LBD. We supplement these links

by matching Employer Identification Numbers and company name, address, and industry in both

data. We merge the Computstat-LBD data with the LEHD files using the Employer Characteristics

Files (ECF). These linking files are widely used in prior literature (e.g., Graham et al., 2016;

Giroud and Mueller, 2017). Finally, we merge with CFRM using CIKs (current and historical).

3.3. Research design and matching

We primarily use a matched sample of fraud and non-fraud firms, except where we explore

accounting quality and wage premiums. We require that these firms be covered by the LEHD data

(i.e., these firms will have at least one existing and one new employee in one of the 23 states) when

examining wages. We first perform a propensity score match within industry-year, using 2-digit

SIC industry codes from the firm-year prior to the AAER-identified misreporting. We estimate the

following cross-sectional probit model on the CFRM-Compustat-LBD-LEHD sample to obtain

firm-year scores to match fraud to non-fraud firms:

17

Fraud-Firm Indicatori,t-1 = β0 + β1 × Sizei,t-1 + β2 × Return on Assetsi,t-1 + β3 × Leveragei,t-1 +

β4 × Tobin’s Qi,t-1 + β5 × Sales Growthi,t-1 + εi,t-1. (1)

We give definitions in the Appendix Table A, and index firm with i and fraud event-time with

t. In Appendix Table B, we report the qualitative results of the probit model. Consistent with prior

literature that matches on size (e.g., Farber, 2005; Schrand and Zechman, 2012), only Size and

Tobin’s Q significantly and positively correlate with Fraud-Firm Indicator.

Our main empirical tests use all observable employees from the fraud and non-fraud firm in

our matched sample. We estimate the following statistical specification characterizing workers’

wages depending on work history (this is a worker-year panel):14

Ln(Annual Real Wagesj,τ) = β1× Pre-Fraud Periodj,τ + β2 × Fraud Periodj,τ +

β3 × Post-Fraud Periodj,τ + β4× Fraud Ind.j × Pre-Fraud Periodj,τ +

β5 × Fraud Ind.j × Fraud Periodj,τ + β6 × Fraud Ind.j × Post-Fraud Periodj,τ +

∑ βm Worker Controlsj,τ + ∑ βk Fixed Effectsj,τ + εj,τ. (2)

We index worker with j and calendar year with τ. Fraud periods vary in calendar time

depending on the worker. Worker controls include interactions of Female Indicator, Education,

and Experience; the main effects are collinear with the fixed effects.15 In all specifications, we

include worker and year fixed effects. We interact industry (and county) fixed effects with the year

effects in some specifications. These controls generally follow Graham et al. (2016) and control

for determinants of wages that could depend on the composition of the fraud and control firms’

workforce and regional, industry-specific shocks. The period indicators span the sample (hence,

14 The panel is not balanced. When we do not observe the worker (e.g., during unemployment for a full year), we

exclude him or her from the sample. We do not infer zero wages, because the worker might have moved to another

state not covered by our project. 15 Experience is collinear with the main effects for the fraud periods (when measured as event-time year indicators),

and we exclude this main effect from those specifications; that is, when Experience is demeaned by worker, it is

effectively equivalent to a sequential count of the number of years in our sample.

18

we do not estimate an intercept). In addition, we estimate specifications where we include event-

time year indicators instead of period indicators.16

This specification is a difference-in-differences approach to estimate the effects of fraudulent

financial reporting. β4 is estimated wages for workers at fraud firms incremental to those at control

firms prior to the misreporting. If the matches are reasonably well chosen, we expect the estimated

coefficient to be insignificantly different from zero and not exhibit any pre-fraud period trends. β5

measures the incremental wages of fraud-firm employees for the fraud period. This measure is our

first coefficient of interest; we infer the consequences for employees during the fraud from this

coefficient estimate. β6 measures the incremental wages for employees of fraud firms during the

post-fraud period. This measure is our second coefficient of interest; we infer the consequences

for employees after the fraud from the coefficient estimate. The identifying assumption for both

of these coefficients is that wages would have evolved (in the absence of fraudulent financial

reporting) for employees of AAER firms during and after the fraud as wages have evolved for

control-firm employees.17

16 Specifically, we include Pre-Fraud Period separately in the regression with indicator variables Pret-4, Pret-3, Pret-

2, and Pret-1. Fraud Period is included with indicators Fraudt, Fraudt+1, and Fraudt+2. Finally, Post-Fraud Period

is included with indicators Postt+3, Postt+4, Postt+5, Postt+6, Postt+7, and Postt+8. Postt+3 is normalized to the first

year after fraud for all sample firms irrespective of the time length of the fraud. 17 In a robustness test, we match employees at fraud firms with random workers at public firms within the same

industry-year. The tradeoff for using this control sample is that we do not rely on the quality of our firm match.

However, the identifying assumption for this alternative control group is that wages would have evolved for

employees of AAER firms during and after the fraud as wages have evolved for these random workers. Yet features

of the firm—for instance, size, growth prospects, or investment efficiency—could be relevant for wages. So

randomly chosen workers could have wage trends that differ due to these unmatched firm characteristics.

19

3.4. Proxies for consequences to employees

As shown in equation (2), we estimate wage effects. We scale wages using the CPI to 2010

price levels.18 We also use employment growth from LBD data to measure firm-wide effects. This

measure indicates dynamic job creation (destruction) across our three periods of fraud.

We perform several sample splits and subsample analyses for descriptive purposes and to

isolate specific economic channels. Our main split is on the period of hire. For an “existing

employee” to be included in tests, we require that she work for the sample firm in the two years

prior to the fraud period, that is, Pret-2 and Pret-1. For a “new employee” to be included in tests,

we require that she not work for the sample firm in the year prior to the fraud period, Pret-1, and

work for the firm for the first year of the fraud period, Fraudt. We also examine “stayers” and

“leavers.” Stayers are with the firm until at least three years into the post-fraud period, Postt+6.

Leavers separate from the firm two years into the post-fraud period, Postt+5, at the latest. For

existing employees who are leavers, we also distinguish between “early leavers” and “late leavers.”

Early leavers separate from the firm during the first year of the fraud period, Fraudt. Late leavers

are all other leavers. Classifying employees as stayers enables us to isolate wage effects from a

continued relationship with the fraud firm apart from the negative consequences from

(unexpectedly) leaving a firm (e.g., Couch and Placzek, 2010). Early leavers are less likely to have

a negatively affected job search from the fraud (or its revelation); late leavers are more likely to

have a negatively affected job search. Therefore, this split, early versus late leavers, differentiates

explanations related to the fraud’s effect on job search.

18 When the data are missing, we do not infer zero wages. This measurement choice will underestimate the costs of

some job switches because we do not include the zeros for workers with long unemployment spells.

20

Finally, we split workers in the top 10% of the pre-fraud, cross-sectional wage distribution

from the bottom 90%. We assume the top wage earners at the firm are much more likely to be

executives and therefore plausibly responsible for the fraudulent financial reporting. We expect

that wage effects for the bottom 90% are not likely the result of direct consequences, namely,

culpability for the misreporting, on the labor market (Fama, 1980; Desai et al., 2006). Instead, we

expect that these workers are primarily affected by a(n unexpected) job search or stigma from the

fraud, without being responsible for it. However, we are unable to observe causes of worker

separations, for instance, layoffs versus plant closings. A separation may have information about

the quality of the worker that we cannot observe (Gibbons and Katz, 1991).

4. Main analyses

4.1. Sample construction and description

Table 1 provides qualitative comparisons of our matched fraud and non-fraud (control) firms.

We perform the matching and measure these differences in the last year of the pre-fraud period.

We match one to one on a firm basis but not an employee basis, so matched firms with different

numbers of employees would result in a larger treatment or control employee sample. We find that

our matching process described in section 3.3 does reasonably well. We do not find significant

differences between fraud and control firms when comparing Size, Return on Assets, Leverage,

Tobin’s Q, Sales Growth, Employment, and Annual Real Wages (LBD). If anything, the fraud firms

appear to be slightly better; signed differences indicate these firms are larger, more profitable, and

have lower leverage, higher investment efficiency / growth prospects, more employees, and lower

(firm-wide) wage bills prior to the fraud; however, none of these differences are statistically

significant.

21

Table 2 describes differences in firm characteristics between fraud firms with LEHD data and

all fraud firms with Compustat data. Firms with employees in more states have a higher likelihood

of entering the LEHD data, so we expect our sample to contain larger and more mature firms,

which it does, according to these signed differences from Table 2. Specifically, our sample fraud

firms are larger, more profitable, have lower leverage, and have lower investment efficiency /

growth prospects. These differences are comparable to similar matching outcomes from prior

literature (e.g., Table 1 Panel B in Graham et al., 2016). Moreover, these differences indicate we

may have some limitations to the generalizability of our results because fraud at larger firms could

be wider reaching and, consequently, have a greater aggregate effect for employees. On the other

hand, larger firms could be more durable and absorb shocks, mitigating effects for employees.

Table 3 describes differences in individual characteristics of existing and new employees of

fraud and control firms. Panel A (Panel B) qualitatively discloses differences for existing (new)

employees in the last year of the pre-fraud period, Pret-1 (first year of the fraud period, Fraudt). At

fraud firms, existing and new employees have relatively similar education, experience, and gender.

New employees at fraud firms are older; existing employees are similar in age. Fraud-firm existing

and new employees do have significantly higher wages. These descriptive wage comparisons are

uncontrolled, first differences; that is, these comparisons are not a difference-in-differences test of

the effects of fraud. We discuss controlled differences in section 4.2 below.

In Table 3, we also measure employee-level attrition in the third year of the post-fraud period,

Postt+6. We generate dummy variables that indicate whether an employee stays working (i) at the

firm, (ii) in the industry, or (iii) in the county. We present qualitative differences for these

indicators for existing and new employees in Panel A and Panel B, respectively. For existing

employees, we observe more attrition for fraud firms across all three indicators. For new

22

employees, we again see attrition, though we do not measure any differences with significance.

Attrition for existing employees is a negative consequence related to fraudulent financial reporting,

particularly if the employee must switch industries or move her location to find new employment

after the fraud.

4.2. Results for wages

As discussed above, firms increase employee levels during restated periods (Kedia and

Philippon, 2009), among other real decisions, such as expanding investment in inefficient ways

(McNichols and Stubben, 2008). We use Census data to replicate this finding for the AAER sample

and show dynamics over the life cycle of the pre-fraud, fraud, and post-fraud periods. In Table 4,

we present qualitative tests of differences for firms’ employment decisions measured as year-on-

year employee growth. We again compare growth at fraud firms with control firms. For these

descriptive tests, we use LBD data. Moreover, we are not constrained by LEHD-participating states

and have a more general sample. We select our control sample using the fraud model from section

3.3. Compared with this control sample, we find positive, significant employee growth among

fraud firms in the pre-fraud period for the two years prior to the fraud, namely, Pret-2 and Pret-1.

The positive employee growth continues throughout the fraud period (though Fraudt+1 is not

significant). Finally, in the post-fraud period, we observe negative employee growth; the

differences are significant in the first two years after the fraud is discontinued, namely, Postt+3 and

Postt+4.

Table 5 contains our main result. We test for dynamic wage effects during and after fraudulent

financial reporting to see the consequences for employees. We present the qualitative description

of coefficient estimates from equation (2) separately for existing and new employees in Panel A

and Panel B, respectively. Across columns in both panels, we increase the number of fixed effects.

23

Specifically, in columns 1, 2, and 3, we estimate models with worker effects and year effects,

industry-year, and industry-county-year effects, respectively. For industry, we use 2-digit SIC

codes. The specification in column 2 controls for industry shocks, and the specification in column

3 controls for regional, industry shocks.

For existing employees (Panel A), in contrast to the univariate results from Table 3, we

observe that employees in the pre-fraud period earn less than workers at non-fraud firms, with

control variables. The significance of this pre-fraud-period difference attenuates statistically in

columns 2 and 3, though the sign is still negative. For the difference-in-differences coefficients of

interest, we find consistently negative wage effects in the fraud and post-fraud periods for

employees who work(ed) at fraud firms. Although we cannot discuss the numeric magnitudes, we

can note two important comparatives within and across specifications. First, within each column,

the magnitudes for the fraud period are greater (in absolute value) than for the pre-fraud period,

and the magnitudes for the post-fraud period are greater (again, in absolute value) than for the

fraud period. That is, the negative wage effect becomes more negative in event-time. Second, the

magnitudes of the coefficients attenuate as additional effects are included; for example, the

coefficients in column 3 are less negative than in column 2. This latter descriptive fact is consistent

with both (i) frauds occurring and being revealed during (regional,) industry shocks and (ii) frauds

being related to industry (and/or regional) spillovers (Beatty et al., 2013) and local labor market

disruptions.

Panel B shows results for new employees. During the pre-fraud period or fraud period, we

find no strong correlations between wages at fraud firms and control firms. However, we again

find that the difference-in-differences estimate for wages in the post-fraud period are negative and

significant. These estimates are only significant in columns 2 and 3, with industry-year and

24

industry-county-year effects, respectively. The same two descriptive facts hold for estimates in

this panel. For coefficients of interest, we see a negative difference between fraud and pre-fraud-

(post-fraud- and fraud-) period estimates. Additionally, we see absolute magnitude attenuation in

our coefficients when we include additional fixed effects. In subsequent analyses, we use worker

and industry-year effects along with other worker controls.

We examine evidence for common trends and robustness to an alternative control group in

Table 6. In Panel A, we split our main coefficients of interest into event-time yearly indicators, as

described above in Footnote 16. We again estimate equation (2) using worker and industry-year

effects and split between existing (column 1) and new (column 2) employees. For existing

employees, we observe minor evidence that wage decreases pre-date the fraud period. The last

year of the pre-fraud period, Pret-1, has a negative and significant coefficient. Otherwise, the

estimated coefficients for the pre-fraud period are not significant (though negative), whereas

coefficients for the fraud and post-fraud periods are negative and significant for all interacted

indicators. For new employees, we see some volatility in the pre-fraud-period wages with a

negative and significant coefficient for Pret-2 but a positive and insignificant coefficient estimate

for Pret-1. The fraud- (post-fraud-) period coefficient estimates are consistently negative and

insignificant (significant). Overall, these tests indicate that the onset of negative wage effects are

relatively sharp and start around the fraud (post-fraud) period for existing (new) employees.

In Panel B, we use an alternative control group without the one-to-one firm match. We

randomly select workers in the same industry at public firms (i.e., with Compustat data) to be the

non-fraud (control) sample. Again, pre-fraud-period trends show relatively stable wages for

existing employees of accounting-fraud firms. New employees have more volatile wage paths in

the pre-fraud period but no obvious trend. Our inferences for the consequences for existing

25

employees are very similar. We measure significant, negative wage effects in the fraud and post-

fraud periods with this alternative control group. For new employees, we see a longer horizon

before they experience negative wage effects compared with randomly matched workers. The

coefficients in the post-fraud period are only statistically significant at Postt+6 and later. Also, we

measure positive coefficients during the fraud period, though only Fraudt is significant.

These analyses in Table 6 show that the negative consequences for employees that we measure

in Table 4 are relatively sharp, coinciding with the fraudulent financial reporting and its revelation.

Additionally, another control sample yields similar inferences for existing employees. Moreover,

long-tenured workers at fraud firms seem to be disproportionately impacted when executives

engage in fraudulent financial reporting, with consistently lower wages during the fraud period.

Measured outcomes for new employees are sensitive to the control group but ultimately show that

they experience negative wage effects in the long run.

5. Mechanism for Wage Effects

5.1. Worker movements

To better understand the source of these wage changes, we descriptively split the result by

worker movements at fraud firms. That is, we separate wage effects in the pre-fraud, fraud, and

post-fraud periods for fraud-firm employees who (i) stay through at least three years in the post-

fraud period (“stayer”), (ii) leave before three years in the post-fraud period (“leaver”), (iii) leave

in the first year of the fraud period (“early leaver”), and (iv) leave after the first year of the fraud

period but before three years in the post-fraud period (“late leaver”). We compare these subsamples

with the average wage effects for workers at non-fraud firms. These results are descriptive because

average wages for control workers include changes from regular job churn. So we caution that

26

workers conditioned on maintaining job status likely have other inherent differences (e.g.,

reliability) that can be consistent with higher wages or positive wage trends. However, these

analyses help us understand where the negative wage effects occur, coinciding with displacements.

In subsequent analyses, we also condition the control group for staying or leaving the firm.

Table 7 shows the qualitative results separated for fraud-firm-employee movements. In

columns 1 and 3 (existing and new employees, respectively), we see that most of the negative wage

effects are experienced by leavers during both the fraud and post-fraud periods. We only find

statistically significant negative wage effects during the fraud period for existing employees, not

new employees. Compared with the average control-firm worker, stayers do all right. In column

2, we find an interesting dynamic for fraud-firm employees who are early versus late leavers. Early

leavers experience negative wage effects during the fraud period (i.e., when they leave the fraud

firm) but afterward have a recovery of wages. Late leavers, on the other hand, have negative wage

effects in both the fraud and post-fraud periods, which is consistent with the revelation of

accounting fraud causing disruption to local labor markets.

In Table 8, we present the qualitative analyses where both fraud-firm employees and control

workers are conditioned on job movements. In Panel A, we examine existing employees and find

that both stayers and leavers have negative wage effects relative to similar stayers and leavers at

control firms. This significant, negative wage effect occurs for both the fraud and post-fraud

periods. We cannot discuss the numeric magnitudes, though we can note that the comparative sizes

of the coefficient estimates for leavers are more negative than for stayers. The negative wage

effects in the post-fraud period are perhaps surprising. Because the fraud has been revealed,

employees want to price protect themselves against newly revealed risks associated with their

employer being a fraud firm. Moreover, the misreporting firm is less likely to be able to absorb

27

idiosyncratic shocks, and employees should want higher wages working for a firm that is less able

to provide “insurance” (Baily, 1974; Guiso et al., 2005). However, other frictions likely prevent

these workers from bargaining for these higher wages; for example, outside options might be worse

due to disrupted local labor markers.19 In Panel B, we examine new employees; we see slight

differences. Stayers have significantly lower wages during the fraud period but insignificantly

lower wages in the post-fraud period; the reverse is true for leavers.

Also in Table 8 column 3, we use a subsample of workers, both at fraud and control firms,

who leave the firm during the first year of the fraud period, Fraudt. That is, these workers leave

before the fraud is revealed. Despite this pre-revelation job switch, former fraud-firm workers

experience negative wage effects in the post-fraud period. We think this evidence is consistent

with a “stigma” effect for these workers. Although they no longer work for the fraud firm and are

not necessarily changing jobs in the post-fraud period, they still experience negative consequences

after the fraud. Another possible explanation is that the new job obtained during the fraud period

was a worse match (compared to new jobs for control workers); however, we do not see significant

negative wage effects during the fraud, that is, when the worker switches. Therefore, the worse

match has a relatively negative pay trend rather than level.

5.2. Wage level

Lastly, in Table 8, we present analyses that condition on the pre-fraud-period wage level

within the firm. We split the sample into workers who are in the top 10% of the wage distribution

(“top 10%”) and the bottom 90% (“non-top 10%”). If highly paid workers are executives who are

19 Kedia and Philippon (2009) show evidence consistent with increased productivity in the post-fraud period for the

GAO restatement sample. It is also perhaps surprising that workers do not see positive wage effects from this

increased productivity or that other effects dominate, causing wages to decline overall.

28

culpable—at least in part—for the misreporting, we expect to have negative wage consequences

concentrated among the top 10% as labor markets “settle up” (Fama, 1980). Non-top 10% workers

are unlikely to have perpetrated the misreporting. So we expect that any wage consequences for

these workers are the result of reorganization, adjustments to unwind inefficient investments,

and/or stigma. In Panel A, existing employees in both the top 10% and non-top 10% groups

experience significant, negative wage effects in the post-fraud period. However, only non-top 10%

employees experience significant, negative effects during the fraud period. We can note that the

absolute magnitudes for non-top 10% employees are greater than for top 10% employees. In Panel

B, new employees in the non-top 10% experience significant, negative wage effects in the post-

fraud period. Otherwise, coefficients are negative but insignificant everywhere. Overall, workers

in the bottom 90% of the wage distribution have worse wage consequences from fraudulent

financial reporting despite the lower likelihood that they are involved with the misreporting.

5.3. Wage premium

Finally, we provide some preliminary evidence on whether wages respond to accounting

quality. We use the absolute value of accruals as a proxy for accounting quality. This proxy has

many documented weaknesses (e.g., Hribar and Nichols, 2007). Although we do not purport to

solve or sidestep these issues, we note that extreme accruals (controlling for firm performance,

prospects, and growth) can be consistent with low accounting quality due to low earnings

persistence or potential manipulation (Dechow et al., 2010). We predict that if workers are

concerned about the likelihood that a firm is misreporting, they will demand wage premiums when

that probability increases. Moreover, workers could anticipate these negative wage consequences

for financial-reporting fraud and price protect against them (e.g., Graham et al., 2016, show similar

29

effects for bankruptcy risk). To test this possibility, we estimate the following specification (we

use a worker-year panel):

Ln(Annual Real Wagesj,τ) = β0 + β1× Accounting Qualityi(j),τ +

∑ βn Firm Controlsi(j),τ + ∑ βm Worker Controlsj,τ + εj,τ. (3)

Firms are indexed by i, workers by j, and years by τ. We show the connection between workers

and firms by notating the firm index as a function. The absolute value of accruals is Accounting

Quality. Firm controls include Size, Return on Assets, Leverage, Tobin’s Q, and Sales Growth.

Worker controls include Female Indicator, Education, Experience, and two-way interactions of

these variables. We use the full sample of LEHD data (i.e., not limited to fraud and control firms).

Table 9 presents descriptive coefficient estimates from the specification above. In addition to

pooling the data, we also split the sample by sales growth; high-sales-growth firms can have more

potential for low-quality earnings or other earnings management (e.g., Dechow, Sloan, and

Sweeney, 1995). Across these tests, we find a positive coefficient on Accounting Quality; however,

this coefficient is only significant in the high-sales-growth subsample. We conclude that weak,

preliminary evidence shows workers demand wage premiums when accounting quality is low. We

caution that positive absolute accruals can also be correlated with other risk factors of the firm

(Hribar and Nichols, 2007), and workers may be responding to other characteristics than

accounting quality. However, if workers have consistent expectations about the negative

consequences of fraud, they should respond to indicators of poor accounting quality. We believe

this area is still open for further analyses and are excited for future exploration.

6. Conclusion

This paper provides evidence on the consequences for employees from fraudulent financial

reporting. We use employer-employee-matched data from the U.S. Census Bureau combined with

30

SEC enforcement actions against firms with serious misreporting (“fraud”) to examine wages and

employee turnover. We find that employees at fraud firms are likely to leave the firm, industry,

and (even) county of employment after the fraud is revealed. We find that employees at fraud firms

have lower wages during and after periods of fraudulent financial reporting even though fraud

firms have higher employment growth before and during the fraud and negative growth after the

fraud is revealed. Sample splits by period of hire show that existing employees have negative

earnings trends during and after the fraud, whereas new employees have negative earnings trends

in the post-fraud period; fraud seems to disproportionately affect long-tenured employees. The

wage effects are robust to a variety of regression specifications.

We argue and show evidence consistent with some specific channels for these wage effects.

The negative change in wages combined with employment growth at fraud firms indicates workers

suffer from firm-specific information asymmetry when executives perpetrate fraudulent financial

reporting. Employees who stay at the fraud firm also have negative wages in the post-fraud period,

so job-switch frictions prevent workers from price protecting themselves from the firm’s riskiness

(e.g., Baily, 1974). Employees who leave also earn less in the post-fraud period, consistent with

(1) shocks affecting firm-specific investments, job search efficiency, and/or entering crowded

labor markets, (2) stigma, and/or, (3) “settling up” from culpability (e.g., Fama, 1980). We

examine early-leaving workers (less affected by 1) and workers in the bottom 90% of the pre-fraud

wage distribution (less affected by 3) and continue to find negative wage effects during and after

fraudulent financial reporting, indicating stigma plays some role even for lower-level employees

(e.g., Groysberg et al., 2017). Finally, we show (weak) evidence that workers require wage

premiums to work for firms with low accounting quality.

31

We note several important caveats. First, we show evidence that could be consistent with

certain hypothesized channels; however, we are unable to isolate the specific effects from any

single channel. For instance, the stigma from the fraud and disruption to labor markets are both

related to the severity of the fraud and any economic shock to the firm plus its fallout.

Consequences for employees can be caused by many explanations even when we perform targeted

sample splits to reduce the likelihood of effects from some channel. Second and related, matched

difference-in-differences designs do not necessarily show causation (Roberts and Whited, 2013).

We find effects that happen concurrently, with little evidence for pre-period trends, so we are

confident these effects are associated with the fraud but not necessarily caused by it. Third, SEC

enforcement priorities could respond to more severe employee consequences rather than neutrally

target cases of serious misreporting. When employees are investors of the firm and suffer

concentrated, negative consequences to their retirement portfolios (e.g., Ball, 2009), the SEC

plausibly views this firm and its executives as an important target for enforcement. So “reverse

causality” could, in part, drive the effects we measure when using AAERs.

We are excited to examine additional areas to address some of these concerns. We plan to

more closely examine employee turnover, measured at the employee level, using the matched

samples in regression analyses and with various splits. We plan to include measures of

unemployment to more fully describe the causes of wage declines. Finally, we plan to use other,

subsequent job changes to try to isolate the stigma effects from fraud. Other areas of interest

include using other samples of (alleged) fraud, for instance, lawsuits or major restatements. We

are also excited to pursue empirical strategies that more closely measure resource-misallocation

effects from fraud-driven information asymmetry.

32

References

Abowd, John J., John Haltiwanger, and Julia Lane. Integrated longitudinal employer-employee

data for the United States.” American Economic Review 94.2 (2004): 224-229.

Abowd, John M., Bryce E. Stephens, Lars Vilhuber, Fredrik Andersson, Kevin L. McKinney,

Marc Roemer, and Simon Woodcock. “The LEHD Infrastructure Files and the Creation of

Quarterly Workforce Indicators.” U.S. Census Bureau, Suitland, MD (2005).

Anderson, Kirsten L., and Teri Lombardi Yohn. “The effect of 10K restatements on firm value,

information asymmetries, and investors’ reliance on earnings.” Working paper (2002).

Autor, David H., David Dorn, Gordon H. Hanson, and Jae Song. “Trade adjustment: Worker-level

evidence.” The Quarterly Journal of Economics 129.4 (2014): 1799-1860.

Baily, Martin Neil. “Wages and employment under uncertain demand.” The Review of Economic

Studies 41.1 (1974): 37-50.

Baker, Scott R. “Debt and the Consumption Response to Household Income Shocks.” Working

paper (2015).

Ball, Ray. “Market and Political/Regulatory Perspectives on the Recent Accounting Scandals.”

Journal of Accounting Research 47.2 (2009): 277-323.

Beatty, Anne, Scott Liao, and Jeff Jiewei Yu. “The spillover effect of fraudulent financial reporting

on peer firms’ investments.” Journal of Accounting and Economics 55.2-3 (2013): 183-205.

Becker, Gary S. “Human capital revisited.” Human Capital: A Theoretical and Empirical Analysis

with Special Reference to Education (3rd Edition). The University of Chicago press, 1994

15-28.

Beneish, Messod D. “Incentives and penalties related to earnings overstatements that violate

GAAP.” The Accounting Review 74.4 (1999): 425-457.

US Bureau of Labor Statistics (BLS). “Quarterly Census of Employment and Wages: Handbook

of Methods.” https://www.bls.gov/cew (2016).

Christensen, Bent Jesper, Rasmus Lentz, Dale T. Mortensen, George R. Neumann, and Axel

Werwatz. “On-the-Job Search and the Wage Distribution.” Journal of Labor Economics 23.1

(2005): 31-58.

Core, John E, and Wayne R. Guay. “Stock option plans for non-executive employees.” Journal of

Financial Economics 61 (2001): 253-287.

Couch, Kenneth A., and Dana W. Placzek. “Earnings losses of displaced workers revisited.”

American Economic Review 100.1 (2010):572-589.

Davis, Steven J., R. Jason Faberman, and John C. Haltiwanger. “The establishment-level behavior

of vacancies and hiring.” The Quarterly Journal of Economics 128.2 (2013): 581-622.

Davis, Steven J., John Haltiwanger, Kyle Handley, Ron Jarmin, Josh Lerner, and Javier Miranda.

“Private Equity, Jobs, and Productivity.” American Economic Review 104.12 (2014): 3956-

3990.

33

Dechow, Patricia M., Weili Ge, Chad R. Larson, and Richard G. Sloan. “Predicting material

accounting misstatements.” Contemporary Accounting Research 28.1 (2011): 17-82.

Dechow, Patricia, Weili Ge, and Catherine Schrand. “Understanding earnings quality: A review

of the proxies, their determinants and their consequences.” Journal of Accounting and

Economics 50.2-3 (2010) 344-401.

Dechow, Patricia M., Richard G. Sloan, and Amy P. Sweeney. “Detecting Earnings Management.”

The Accounting Review 70.2 (1995): 193-225.

Desai, Hemang, Chris E. Hogan, and Michael S. Wilkins. “The reputation penalty for aggressive

accounting: Earnings restatements and management turnover.” The Accounting Review 81.1

(2006): 83-112.

Dyck, Alexander, Adair Morse, and Luigi Zingales. “How pervasive is corporate fraud?” Working

paper (2013).

Erickson, Merle, Michelle Hanlon, and Edward L. Maydew. “How Much Will Firms Pay for

Earnings That Do Not Exist? Evidence of Taxes Paid on Allegedly Fraudulent Earnings.”

The Accounting Review 79.2 (2004): 387-408.

Fama, Eugene F. “Agency problems and the theory of the firm.” Journal of Political Economy

88.2 (1980): 288-307.

Farber, David B. “Restoring Trust after Fraud: Does Corporate Governance Matter?” The

Accounting Review 80.2 (2005): 539-561.

Feroz, Ehsan H., Kyungjoo Park, and Victor S. Pastena. “The financial and market effects of the

SEC’s accounting and auditing enforcement releases.” Journal of Accounting Research 29

Supplement (1991): 107-142.

Gathmann, Christina, and Uta Schonberg. “How General Is Human Capital? A Task-Based

Approach.” Journal of Labor Economics 28.1 (2010): 1-49.

Gibbons, Robert, and Lawrence F. Katz. “Layoffs and Lemons.” Journal of Labor Economics 9.4

(1991): 351-380.

Giroud, Xavier, and Holger M. Mueller. “Firm leverage, consumer demand, and employment

losses during the Great Recession.” The Quarterly Journal of Economics 132.1 (2017): 271-

316.

Graham, John R., Hyunseob Kim, Si Li, and Jiaping Qiu. “Employee Costs of Corporate

Bankruptcy.” Working paper (2016).

Groysberg, Boris, Eric Lin, and George Serafeim. “Does Financial Misconduct Affect the Future

Compensation of Alumni Managers?” Working paper (2017).

Guiso, Luigi, Luigi Pistaferri, and Fabiano Schivardi. “Insurance within the Firm.” Journal of

Political Economy 113.5 (2005): 1054-1087.

Hribar, Paul, and Nichols, D. Craig. “The Use of Unsigned Earnings Quality Measures in Tests of

Earnings Management.” Journal of Accounting Research 45.5 (2007): 1,017–1,053.

Hummels, David, Rasmus Jorgensen, Jakob Munch, and Chong Xiang. “The Wage Effects of

Offshoring: Evidence from Danish Matched Worker-Firm Data.” American Economic

Review 104.6 (2014): 1597-1629.

34

Hyatt, Henry, and Ericka McEntarfer. “Job-to-Job Flows in the Great Recession.” American

Economic Review: Papers & Proceedings 102.3 (2012): 580-583.

Jacobson, Louis S., Robert J. LaLonde, and Daniel G. Sullivan. “Earnings Losses of Displaced

Workers.” American Economic Review 83.4 (1993): 685-709.

Jovanovic, Boyan. “Job matching and the theory of turnover.” Journal of Political Economy 87.5,

Part 1 (1979a): 972-990.

Jovanovic, Boyan. “Firm-specific Capital and Turnover.” Journal of Political Economy 87.6

(1979b): 1246-1260.

Karpoff, Jonathan M., Allison Koester, D. Scott Lee, and Gerald S. Martin. “Proxies and Databases

in Financial Misconduct Research.” The Accounting Review 92.6 (2017): 129-163.

Karpoff, Jonathan M., D. Scott Lee, and Gerald S. Martin. “The consequences to managers for

financial misrepresentation.” Journal of Financial Economics 88.2 (2008a): 193.215

Karpoff, Jonathan M., D. Scott Lee, and Gerald S. Martin. “The cost to firms of cooking the

books.” Journal of Financial and Quantitative Analysis 43.3 (2008): 581-611.

Kedia, Simi, and Thomas Philippon. “The Economics of Fraudulent Accounting.” The Review of

Financial Studies 22.6 (2009): 2169-2199.

Liberto, Jennifer. “House passes bipartisan bill aimed at start-ups.” CNN Money (2012).

Leuz, Christian. “Evidence-Based Policymaking: Promise, Challenges and Opportunities for

Accounting and Financial Markets Research.” Working paper (2018).

Manning, Alan. “Imperfect Competition in the Labor Market.” Handbook of Labor Economics 4b

(2011): 937-1041.

McNichols, Maureen F., and Stephen R. Stubben. “Does Earnings Management Affect Firms’

Investment Decisions?” The Accounting Review 83.6 (2008): 1571-1603.

Mortensen, Dale T., and Christopher A. Pissarides. “New developments in models of search in the

labor market.” Handbook of Labor Economics 3 (1999): 2567-2627.

Neal, Derek. “Industry-Specific Human Capital: Evidence from Displaced Workers.” Journal of

Labor Economics 13.4 (1995): 653-677.

Roberts, Michael R., and Toni M. Whited. “Chapter 7: Endogeneity in Empirical Corporate

Finance.” Handbook of the Economics of Finance Vol. 2. Elsevier, 2013. 493-572.

Samaniego de la Parra, Brenda. “Formal Firms, Informal Workers, and Household Labor Supply:

Evidence from Mexico.” Working paper (2018).

Schrand, Catherine M., and Sarah LC Zechman. “Executive overconfidence and the slippery slope

to financial misreporting.” Journal of Accounting and Economics 53.1-2 (2012): 311-329.

Silva, Rui. “Internal Labor Markets and Investment in Conglomerates.” Working paper (2013).

Srinivasan, Suraj. “Consequences of Financial Reporting Failure for outside Directors: Evidence

from Accounting Restatements and Audit Committee Members.” Journal of Accounting

Research 43.2 (2005): 291-334.

35

Tate, Geoffrey, and Liu Yang. “The bright side of corporate diversification: Evidence from internal

labor markets.” The Review of Financial Studies 28.8 (2015): 2203-2249.

Walker, W. Reed. “The transitional costs of sectoral reallocation: Evidence from the clean air act

and the workforce.” The Quarterly Journal of Economics 128.4 (2013): 1787-1835.

Wilson, Wendy M. “An Empirical Analysis of the Decline in the Information Content of Earnings

Following Restatements.” The Accounting Review 83.2 (2008): 519-548.

36

Appendix Table A: Variable Definitions

Variable Definition Data

Source

Dependent Variables

Employment The number of employees at the end of a year LBD

Annual Real

Wages

Annual earnings from a primary employer divided by the

Consumer Price Index (2010)

LEHD

Avg. Annual

Real Wages

Total wage bill divided by employment LBD

Fraud Firm

Indicator

Companies that are identified as accounting-fraud firms by the

AAER from 1970 through 2014

CFRM,

AAERs

Independent Variables

Fraud

Indicator

Workers who are at fraud firms as either an Existing Employee or

a New Employee

LEHD

Pre-Fraud 1 if year t falls within four years before a fraud firm engaged in

accounting fraud; 0 otherwise

CFRM,

AAERs

Fraud 1 if year t falls when a fraud firm engaged in accounting fraud, 0

otherwise

CFRM,

AAERs

Post-Fraud 1 if year t falls within six years after an accounting fraud is

revealed; 0 otherwise

CFRM,

AAERs

Sample Splits

Existing

Employee

Worker at a fraud or control firm for the last two years before a

fraud firm engaged in accounting fraud, Pret-2 and Pret-1

LEHD

New Employee Worker newly hired in the first year of a fraud period, Fraudt, by

a fraud or control firm

LEHD

Stayer /

Leaver

Stayer if an employee continues to work for the fraud or control

firm three years after the accounting fraud is revealed, Postt+6

and/or later; leaver otherwise

LEHD

Early / Late

Leaver

Early leaver if an employee left the fraud or control firm in the

first year of accounting fraud, Fraudt; late leaver if the fraud or

control firm in any other year of accounting fraud or within two

years after accounting fraud is revealed, Fraudt+1 through Postt+5.

LEHD

Top 10% Workers earn real wages more than or equal to the 10 percentile

real wage in the wage distribution

LEHD

Non-Top 10% Workers earn real wages less than the 10 percentile real wage in

the wage distribution

LEHD

37

Appendix Table A: Variable Definitions (continued)

Variable Definition Data

Source

Firm Controls

Size Natural log of total sales (data6) Compustat

Return on

Assets

Operating income after depreciation (data178) divided by total

assets (data6)

Compustat

Leverage The ratio of total debt (data9+data34) to market value of assets,

which is calculated by multiplying the number of shares

outstanding (data25) by the stock price (data199) and by adding

total debt (data9+data34) to it

Compustat

Tobin’s Q Market value of assets divided by book value of assets (data6),

where market value of assets is calculated by

(data25*data199+data9+data34)

Compustat

Sales

Growth

Natural log of this year’s sales minus natural log of last year’s

sales (data12)

Compustat

Employee Controls

Age Age of an employee in an event year of accounting fraud LEHD

Education Four levels of education are transformed into numerical values by

using the highest number of years in each category: less than high

school (1-8), high school or equivalent, no college (9), some

college or associate degree (10-12), and bachelor’s degree or

advanced degree (13-16)

LEHD

Experience Age of a worker in year t minus education minus 6 LEHD

Female 1 if a person is female; 0 otherwise LEHD

38

Appendix Table B: Probit Model

This table shows the results of a probit model estimating a propensity score to engage in accounting fraud. Accounting-

fraud firms are identified by the AAER. Fraud firms are included in sample firms in the year prior to accounting fraud,

Pret-1. Non-fraud firms are included in sample firms if they operate businesses in the same industry as one of fraud

firms in the year prior to accounting fraud. The sample period is from 1991 to 2008. Appendix Table A defines

variables. Statistical significance at the 10%, 5%, and 1% levels is indicated by *, **, and ***, respectively.

Significance below these conventional levels is indicated with “ns.” Descriptive statistics, coefficient estimates, t-

statistics, number of observations, and R-squared will be reported after receiving permission from the U.S. Census

Bureau that the output complies with disclosure requirements. For now, tables include qualitative disclosures,

including sign and conventional significance levels.

(1) (2)

Dependent Variable: Fraud-Firm Indicator Sign Significance

Size + ***

Return on Assets - ns

Leverage + ns

Tobin’s Q + ***

Sales Growth - ns

Observations

R-squared

39

Table 1. Comparison of Fraud and Matched Control Firms

This table compares fraud firms’ to control firms’ characteristics in the year prior to accounting fraud, Pret-1.

Accounting-fraud firms are identified by the AAER. Control firms are matched to fraud firms based on a propensity

score estimated in Appendix Table B. The sample period is from 1991 to 2008. Appendix Table A defines variables.

Statistical significance at the 10%, 5%, and 1% levels is indicated by *, **, and ***, respectively. Significance below

these conventional levels is indicated with “ns.” Descriptive statistics, coefficient estimates, t-statistics, number of

observations, and R-squared will be reported after receiving permission from the U.S. Census Bureau that the output

complies with disclosure requirements. For now, tables include qualitative disclosures, including sign and

conventional significance levels.

(1) (2) (3)

Fraud

Firms

Non-Fraud

Firms

T Tests of Differences

(Fraud minus Non-Fraud)

Sign Significance

Size + ns

Return on Assets + ns

Leverage - ns

Tobin’s Q + ns

Sales growth + ns

Employment + ns

Avg. Annual Real Wages (LBD) - ns

Observations

40

Table 2. Descriptive Statistics on Fraud Firms

This table compares statistics on samples of fraud firms. Column (1) indicates descriptive statistics of sample fraud

companies, and column (2) indicates descriptive statistics of all fraud firms. Column (3) indicates signed differences

between columns 1 and 2. Fraud firms are identified by the AAER. All fraud companies are required to have relevant

Compustat data. They engaged in accounting fraud from 1970 to 2014. Sample fraud companies are required to have

relevant Compustat, LBD, and LEHD data. They engaged in accounting fraud from 1991 to 2008. Appendix Table A

defines variables. Descriptive statistics, coefficient estimates, t-statistics, number of observations, and R-squared will

be reported after receiving permission from the U.S. Census Bureau that the output complies with disclosure

requirements. For now, tables include qualitative disclosures, including sign and conventional significance levels.

(1) (2) (3)

Sample Fraud

Firms

All Fraud

Firms

Signs of Differences

(Sample minus All)

Sign

Size +

Return on Assets +

Leverage -

Tobin’s Q -

Sales growth -

Observations

41

Table 3. Descriptive Statistics on Employees of Fraud and Control Firms

This table shows qualitative differences for averages of employees at fraud and control firms. Accounting-fraud firms

in the sample commit financial misrepresentation from 1991 to 2008 according to the AAER. Fraud firms are matched

with control firms using a propensity score estimated in Appendix Table B. Panel A limits the sample to existing

employees. Panel B limits the sample to new employees. % Stay at Firm, in Industry, and in County are measured by

calculating the proportion of workers who continue to work for the same firm, industry, and county as in an event year

of accounting fraud three years after accounting fraud is revealed (Postt+6), respectively. Appendix Table A defines

variables. Statistical significance at the 10%, 5%, and 1% levels is indicated by *, **, and ***, respectively.

Significance below these conventional levels is indicated with “ns.” Descriptive statistics, coefficient estimates, t-

statistics, number of observations, and R-squared will be reported after receiving permission from the U.S. Census

Bureau that the output complies with disclosure requirements. For now, tables include qualitative disclosures,

including sign and conventional significance levels.

Panel A: Existing Employees

(1) (2) (3) (4)

Fraud

Firms

Non-Fraud

Firms

T-Test of Differences

(Fraud minus Non-Fraud)

Sign Significance

Education + ns

Age + ns

Experience + ns

Annual Real Wages + **

Female + ns

% Stay at Firm - *

% Stay in Industry - *

% Stay in County - ***

Observations

Panel B: New Employees

(1) (2) (3) (4)

Fraud

Firms

Non Fraud

Firms

T-Test of Differences

(Fraud minus Non-Fraud)

Sign Significance

Education + ns

Age + *

Experience + ns

Annual Real Wages + **

Female - ns

% Stay at Firm - ns

% Stay in Industry - ns

% Stay in County - ns

Observations

42

Table 4. Dynamics of Employment Growth of Fraud Firms (LBD Data)

This table shows qualitative differences for averages of employment growth at fraud and control (non-fraud) firms.

Accounting-fraud firms in the sample commit financial misrepresentation from 1991 to 2008 according to the AAER.

Fraud firms are matched with control firms using a propensity score estimated in Appendix Table B. Employment

growth is the natural log of employment this year minus the natural log of employment last year. The sample period

is from three years before a firm engages in accounting fraud, Pret-3, through three years after accounting fraud is

revealed, Postt+5. Statistical significance at the 10%, 5%, and 1% levels is indicated by *, **, and ***, respectively.

Significance below these conventional levels is indicated with “ns.” Descriptive statistics, coefficient estimates, t-

statistics, number of observations, and R-squared will be reported after receiving permission from the U.S. Census

Bureau that the output complies with disclosure requirements. For now, tables include qualitative disclosures,

including sign and conventional significance levels.

(1) (2) (3) (4)

Fraud

Firms

Non-Fraud

Firms

T-Test of Differences

(Fraud minus Non-Fraud)

Sign Significance

Pret-3 + ns

Pret-2 + **

Pret-1 + *

Fraudt + **

Fraudt+1 + ns

Fraudt+2 + ***

Postt+3 - *

Postt+4 - **

Postt+5 - ns

Observations

43

Table 5. Effect of Accounting Fraud on Employee Earnings

This table reports qualitative estimates from OLS regression analyses estimating equation (2): estimates for wage effects at fraud firms in the pre-fraud, fraud, and

post-fraud periods. Accounting-fraud firms in the sample commit financial misrepresentation from 1991 to 2008 according to the AAER. Fraud firms are matched

with control firms using a propensity score estimated in Appendix Table B. Panel A limits the sample to existing employees. Panel B limits the sample to new

employees. Appendix Table A defines variables. Statistical significance at the 10%, 5%, and 1% levels is indicated by *, **, and ***, respectively. Significance

below these conventional levels is indicated with “ns.” Descriptive statistics, coefficient estimates, t-statistics, number of observations, and R-squared will be

reported after receiving permission from the U.S. Census Bureau that the output complies with disclosure requirements. For now, tables include qualitative

disclosures, including sign and conventional significance levels.

Panel A: Existing Employees

(1) (2) (3)

Dependent Variable =

Ln(Annual Real Wages) Sign Significance Sign Significance Sign Significance

Pre-Fraud × Fraud Ind. - * - ns - ns

Fraud × Fraud Ind. - * - *** - **

Post-Fraud × Fraud Ind. - * - ** - ***

Female Ind. × Experience + ** + ns - ***

Experience × Education + *** + *** + ***

Main effects Yes Yes Yes

Fixed Effects Year,

Worker

Year ×

Industry,

Worker

Year ×

Industry ×

County,

Worker

Observations

R-squared

44

Table 5. Effect of Accounting Fraud on Employee Earnings (Continued)

Panel B: New Employees

(1) (2) (3)

Dependent Variable =

Ln(Annual Real Wages) Sign Significance Sign Significance Sign Significance

Pre-Fraud × Fraud Ind. + ns - ns - ns

Fraud × Fraud Ind. - ns - ns - ns

Post-Fraud × Fraud Ind. - ns - *** - ***

Female Ind. × Experience + ns - ns - ns

Experience × Education + *** + *** + ***

Main effects Yes Yes Yes

Fixed Effects Year,

Worker

Year ×

Industry,

Worker

Year ×

Industry ×

County,

Worker

Observations

R-squared

45

Table 6. Dynamics of Employee Earnings of Fraud Firms

This table reports qualitative estimates from OLS regression analyses estimating equation (2): estimates for wage

effects at fraud firms in the by-event-time years. Accounting-fraud firms in the sample commit financial

misrepresentation from 1991 to 2008 according to the AAER. In Panel A, control firms are matched with fraud firms

using a propensity score estimated in Appendix Table B. In Panel B, 1% of employees of other public companies in

the same industry are randomly selected as employees of control firms. Appendix Table A defines variables. Statistical

significance at the 10%, 5%, and 1% levels is indicated by *, **, and ***, respectively. Significance below these

conventional levels is indicated with “ns.” Descriptive statistics, coefficient estimates, t-statistics, number of

observations, and R-squared will be reported after receiving permission from the U.S. Census Bureau that the output

complies with disclosure requirements. For now, tables include qualitative disclosures, including sign and

conventional significance levels.

Panel A: Probit-Matched Control-Firm Employees

(1) (2)

Existing

Employees

New

Employees

Dependent Variable =

Ln(Annual Real Wages) Sign Significance Sign Significance

Pret-4 × Fraud Ind. - ns - ns

Pret-3 × Fraud Ind. - ns - ns

Pret-2 × Fraud Ind. - ns - **

Pret-1 × Fraud Ind. - ** + ns

Fraudt × Fraud Ind. - *** - ns

Fraudt+1 × Fraud Ind. - ** - ns

Fraudt+2 × Fraud Ind. - ** - ns

Postt+3 × Fraud Ind. - *** - *

Postt+4 × Fraud Ind. - *** - **

Postt+5 × Fraud Ind. - *** - ***

Postt+6 × Fraud Ind. - ** - ***

Postt+7 × Fraud Ind. - ** - ***

Postt+8 × Fraud Ind. - * - *

Controls and main effects Yes Yes

Fixed Effects

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Observations

R-squared

46

Table 6. Dynamics of Employee Earnings of Fraud Firms (continued)

Panel B: Random Industry-Matched Control Workers

(1) (2)

Existing

Employees

New

Employees

Dependent Variable =

Ln(Annual Real Wages) Sign Significance Sign Significance

Pret-4 × Fraud Ind. - ns + *

Pret-3 × Fraud Ind. + ns + ns

Pret-2 × Fraud Ind. + ns - *

Pret-1 × Fraud Ind. - ns + ns

Fraudt × Fraud Ind. - *** + **

Fraudt+1 × Fraud Ind. - ** + ns

Fraudt+2 × Fraud Ind. - ** + ns

Postt+3 × Fraud Ind. - *** + ns

Postt+4 × Fraud Ind. - *** - ns

Postt+5 × Fraud Ind. - *** - ns

Postt+6 × Fraud Ind. - *** - *

Postt+7 × Fraud Ind. - *** - *

Postt+8 × Fraud Ind. - ** - *

Controls and main effects Yes Yes

Fixed Effects

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Observations

R-squared

47

Table 7. Descriptive Earnings Changes across Fraud-Firm Employee Movements

This table reports qualitative estimates from OLS regression analyses estimating a modified version of equation (2) with fraud-firm employee movement splits:

estimates for wage effects at fraud firms in the pre-fraud, fraud, and post-fraud periods. Accounting-fraud firms in the sample commit financial misrepresentation

from 1991 to 2008 according to the AAER. Fraud firms are matched with control firms using a propensity score estimated in Appendix Table B. Columns (1) and

(2) limit the sample to existing employees. Column (3) limits the sample to new employees. Appendix Table A defines variables. Statistical significance at the

10%, 5%, and 1% levels is indicated by *, **, and ***, respectively. Significance below these conventional levels is indicated with “ns.” Descriptive statistics,

coefficient estimates, t-statistics, number of observations, and R-squared will be reported after receiving permission from the U.S. Census Bureau that the output

complies with disclosure requirements. For now, tables include qualitative disclosures, including sign and conventional significance levels.

(1) (2) (3)

Existing Employees New Employees

Stayers v.

Leavers

Early v.

Late Leavers

Stayers v.

Leavers

Dependent Variable =

Ln(Annual Real Wages) Sign Sig. Sign Sig. Sign Sig.

Pre-Fraud × Fraud Ind. × Stayer - ** - ** - ***

Pre-Fraud × Fraud Ind. × Leaver - ns . . + ns

Pre-Fraud × Fraud Ind. × Early Leaver . . + ns . .

Pre-Fraud × Fraud Ind. × Late Leaver . . - ns . .

Fraud × Fraud Ind. × Stayer + ns + ns + ns

Fraud × Fraud Ind. × Leaver - *** . . - ns

Fraud × Fraud Ind. × Early Leaver . . - ** . .

Fraud × Fraud Ind. × Late Leaver . . - ** . .

Post-Fraud × Fraud Ind. × Stayer + ns + ns + ns

Post-Fraud × Fraud Ind. × Leaver - *** . . - ***

Post-Fraud × Fraud Ind. × Early Leaver . . + ns . .

Post-Fraud × Fraud Ind. × Late Leaver . . - ** . .

Controls and main effects Yes Yes Yes

Fixed Effects

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Observations

R-squared

48

Table 8. Earnings Changes Conditional on Worker Movement and Pre-Fraud Wage Levels

This table reports qualitative estimates from OLS regression analyses estimating equation (2): estimates for wage effects at fraud firms in the pre-fraud, fraud, and

post-fraud periods. Across columns, we limit the sample to various subsamples conditional on worker movements and pre-fraud wage levels. Panel A limits the

sample to existing employees. Panel B limits the sample to new employees. Column headers indicate the conditional group of workers included in the analysis.

Accounting-fraud firms in the sample commit financial misrepresentation from 1991 to 2008 according to the AAER. Fraud firms are matched with control firms

using a propensity score estimated in Appendix Table B. Appendix Table A defines variables. Statistical significance at the 10%, 5%, and 1% levels is indicated

by *, **, and ***, respectively. Significance below these conventional levels is indicated with “ns.” Descriptive statistics, coefficient estimates, t-statistics, number

of observations, and R-squared will be reported after receiving permission from the U.S. Census Bureau that the output complies with disclosure requirements. For

now, tables include qualitative disclosures, including sign and conventional significance levels.

Panel A: Existing Employees

(1) (2) (3) (4) (5)

Stayers Leavers Early

Leavers

Top 10%

Earners

Non-top

10%

Earners

Dependent Variable =

Ln(Annual Real Wages) Sign Sig. Sign Sig. Sign Sig. Sign Sig. Sign Sig.

Pre-Fraud - ns - * - ns - ns - ns

Fraud - * - ** - ns - ns - ***

Post-Fraud - * - *** - * - ** - **

Controls and main effects Yes Yes Yes Yes Yes

Fixed Effects

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Observations

R-squared

49

Table 8. Earnings Changes Conditional on Worker Movement and Pre-Fraud Wage Levels (continued)

Panel B: New Employees

(1) (2) (3) (4)

Stayers Leavers Top 10%

Earners

Non-top

10%

Earners

Dependent Variable =

Ln(Annual Real Wages) Sign Sig. Sign Sig. Sign Sig. Sign Sig.

Pre-Fraud - ns - ns - ns - ns

Fraud - * - ns - ns - ns

Post-Fraud - ns - *** - ns - **

Controls and main effects Yes Yes Yes Yes

Fixed Effects

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Year ×

Industry,

Worker

Observations

R-squared

50

Table 9. Wage Premiums and Fraud Characteristics

This table reports qualitative estimates from OLS regression analyses estimating equation (3): estimates for wage premiums and accounting quality. Column (1)

reports results for the full sample of employees at public companies. Columns (2) and (3) report results for employees of high- and low-growth firms, respectively,

split at the sample median for Sales Growth. We use 1% of employees of public companies, sampled from 1985 to 2014. Employees are 20 to 55 years old. Their

annual real wages are higher than $2,000. Appendix Table A defines variables. Statistical significance at the 10%, 5%, and 1% levels is indicated by *, **, and

***, respectively. Significance below these conventional levels is indicated with “ns.” Descriptive statistics, coefficient estimates, t-statistics, number of

observations, and R-squared will be reported after receiving permission from the U.S. Census Bureau that the output complies with disclosure requirements. For

now, tables include qualitative disclosures, including sign and conventional significance levels.

(1) (2) (3)

High Growth

Firms

Low Growth

Firms

Dependent Variable =

Ln(Annual Real Wages) Sign Significance Sign Significance Sign Significance

Accounting Quality

(Absolute Accruals) + ns + * + ns

Size + *** + *** + ***

Return on Assets - *** - *** - ***

Leverage - * - * - *

Tobin’s Q + *** + *** + ***

Sales Growth + *** + *** - ns

Female Indicator - *** - *** - ***

Education + *** + *** + ***

Experience + *** + *** + ***

Female Ind. × Experience - *** - *** - ***

Female Ind. ×Education - *** - *** - ***

Experience × Education + *** + *** + ***

Observations

R-squared

51

Figure 1: A Fraud Example, Timeline, and Employees

Fraud Firm Timeline:

Pre-Fraud Period Fraud Period Post-Fraud Period

Pret-4 Pret-3 Pret-2 Pret-1 Fraudt Fraudt+1 Fraudt+2 Postt+3 Postt+4 Postt+5 Postt+6 Postt+7 Postt+8

Employee Types:

Existing Employee New Employee

This figure is a representation of the accounting-fraud timeline. The fraud is split into three periods. The “Pre-Fraud Period” extends for

up to four years prior to the beginning of the fraud from the Accounting and Auditing Enforcement Release (AAER). We indicate these

years as Pret-4, Pret-3, Pret-2, and Pret-1. The “Fraud Period” extends for the length of the fraud and must result in misreporting of an

annual financial statement (e.g., a single quarter of fraud that is corrected within a fiscal year would be excluded). The Fraud Period is

determined by the start year and end year of financial misrepresentation from the AAER. We indicate these years as Fraudt, Fraudt+1,

and Fraudt+2. When indicating event-time years, we normalize this period to a maximum of three years by indicating additional fraud

years as Fraudt+2. The “Post-Fraud Period” extends for up to six years after the conclusions of the fraud from the AAER. We indicate

these years as Postt+3, Postt+4, Postt+5, Postt+6, Postt+7, and Postt+8.

We classify employees into two types. “Existing Employees” are workers at fraud (or control) firms prior to the beginning of the fraud

indicated in the AAER. We require that existing employees worked for a fraud firm or a control firm for the last two years before a fraud

firm engaged in accounting fraud, Pret-2 and Pret-1. We do not require that we are able to observe the hire date if the employee works

for the firm before our sample begins. “New Employees” are workers at fraud (or control) firms hired during the Fraud Period. We

require that new employees were hired in the first year of a fraud period by a fraud firm or a control firm, Fraudt.