Do Retail Investors Understand Restatements? Evidence from Trading Around Fraud vs. Non-Fraud Restatements *

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1 Do Retail Investors Understand Restatements? Evidence from Trading Around Fraud vs. Non-Fraud Restatements * Yifan Li Devin Shanthikumar The Paul Merage School of Business University of California, Irvine August 26, 2016 Abstract The spike in restatements in the early 2000s prompted an important question: Are retail investors able to react to the large volume of restatements, and in particular are they able to differentiate between non-fraud restatements and more serious fraud-related restatements? The latter are associated with more negative announcement-window and post-announcement returns. Using a unique dataset, we directly examine retail investor trading reactions to restatement announcements. We find that retail investors display significantly higher trading volumes during restatementannouncement windows, as well as significantly higher abnormal trading volume for fraud-related restatements than for non-fraud restatements. However, retail investors increase both their buying and selling, and do not sell any more strongly as a percentage of trade for fraud- versus non-fraudrelated restatements. We examine the returns following retail investors trades and find that retail investors share purchases for fraud-related restatements earn significantly negative raw and abnormal returns (e.g., -8% raw returns over three months). This suggests that retail investors failure to differentiate between fraud- and non-fraud-related restatements may have significant welfare consequences. We further examine the potential role of press coverage and find that retail investors sell more strongly for fraud-related restatements when restatements receive more press coverage. However they continue to buy significantly for fraud-related restatements even when press coverage is high, which leads to subsequent negative returns. Overall, our results suggest that retail investors fail to understand the negative implications of fraud-related restatements. Keywords: restatement, fraud, retail investor, small investor, individual investor, investor behavior JEL Classifications: M41, G14, D83 * We thank Kevin Chu, Cody Lu, Jonathon Shaw, and Aruhn Venkat for research assistance. We thank Tiana Lehmer, Mort Pincus, two anonymous conference reviewers, and seminar participants at the University of California, Irvine for helpful comments. Send correspondence to dshanthi@uci.edu. Phone: Mailing address: The Paul Merage School of Business, University of California Irvine, Irvine CA

2 1. Introduction Investors rely on information in quarterly and annual financial statements when making decisions, yet these reports are not always correct. Around the time of the Sarbanes-Oxley Act of 2002 (SOX), the United States experienced a dramatic increase in the number of financial report restatements filed with the Securities and Exchange Commission (SEC). In 1997, 69 restatements were filed by exchange-listed companies. By 2005, this number was 753 (Scholz 2008). However, it is an open question whether this increase in restatement reporting is beneficial to small investors. On one hand, more information is useful if the market is able to fully process such information. On the other hand, if investors face processing constraints, then information overload may occur, and they may fail to identify which restatements are truly egregious. Growing evidence of limited investor attention (e.g., Barber and Odean 2008) and the impact of limited attention on the market response to information (e.g., DellaVigna and Pollet 2009; Hirshleifer, Lim, and Teoh 2009) supports the idea that information overload is a potential concern. Over the same 1997-through period, the number of fraud-related restatements increased only slightly, from 26 in 1997 to 36 in Can the average investor identify 36 fraud-related restatements among a set of 753, or are investors overwhelmed by this information? Fraud- and irregularity-related restatements ( fraud-related restatements ) are followed by significantly negative abnormal returns (Burks 2011), higher rates of CEO and CFO turnover (Hennes, Leone, and Miller 2008), and a wide range of reputation-building actions (Chakravarthy, dehaan, and Rajgopal 2014). Non-fraud restatements, in contrast, are often related to technical accounting errors and have less significant consequences. Hennes, Leone, and Miller (2008) highlight the importance of distinguishing between these two types of restatements in research. Being able to distinguish between them is likely to be important for investors as well. While prior 1

3 literature has shown that the market reacts with more negative announcement-window returns for fraud-related restatements (Scholz 2008; Burks 2011), less sophisticated retail investors may not differentiate. As we discuss below, there are reasonable arguments for either prediction: that retail investors do, or do not, differentiate. Given the SEC s focus on individual investor welfare, 1 and its renewed focus on identifying and combatting financial reporting fraud with the 2013 creation of the Financial Reporting and Audit Task Force (Ceresney 2013; SEC 2013b, 2016), understanding individual investor reactions to restatements, and particularly fraud, is important. The examination of retail investor reactions in this setting also provides us with unique insights into retail investor behavior. Prior research on retail investors has shown that they react in simplistic or naïve ways around earnings announcements. 2 Yet interpreting an earnings announcement requires accounting and business knowledge that many investors may lack. In contrast, a restatement involving fraud is almost unambiguously bad, if a retail investor is able to identify it as such. In addition, the majority of earlier research uses retail trading data prior to Studies using more recent data find that retail investor trading positively predicts future returns (Kaniel, Saar, and Titman 2008; Kaniel, Liu, Saar and Titman 2012; Kelley and Tetlock 2008), suggesting that retail investors may be more sophisticated than previously thought. Thus our results also speak to a potential shift in retail investor sophistication (Kelley and Tetlock 2008). Using a unique dataset capturing all retail investor trading on the New York Stock Exchange (NYSE) over the period, we directly examine retail investor trading reactions to restatement announcements. Prior literature on individual investor trading has largely been 1 The SEC writes, prominently, The mission of the U.S. Securities and Exchange Commission is to protect investors, maintain fair, orderly, and efficient markets, and facilitate capital formation. As more and more first-time investors turn to the markets to help secure their futures, pay for homes, and send children to college, our investor protection mission is more compelling than ever (SEC 2013a). 2 See, for example, Battacharya (2001), Battalio and Mendenhall (2005), Allee, Bhattacharya, Black, and Christensen (2007), Bhattacharya, Black, Christensen, and Mergenthaler (2007), and Shanthikumar (2012). 2

4 constrained to earlier time periods due to data restrictions. Our analysis focuses on over 650 restatements from this recent time period. While we lack comparable data for other groups of investors, we also examine overall market returns. Extending return results to our more recent sample, we find results consistent with Palmrose, Richardson, and Scholz (2004), Scholz (2008), and Burks (2011). In particular, we find that returns are significantly more negative for restatements associated with fraud than those not associated with fraud, for both the announcement window (-3.9% vs. -0.9%) and the six months post-announcement (-8.5% vs. 0.9%). This implies that investors should sell upon the announcement of a fraud-related restatement if they want to avoid predictable losses. This also suggests that at least some part of the market distinguishes the two types of restatements at the announcement date, but at least some part of the market fails to fully react to the negative signal initially. While in general a delayed reaction may be due in part to residual uncertainty at the announcement date, investors should not be willing to pay predictably negative average returns to wait for the resolution of uncertainty. If anything, increased uncertainty should have the opposite effect (e.g. Kumar, Sorescu, Boehme and Danielsen 2008). Thus the negative drift is surprising, and suggests that at least some investors may be failing to fully respond to restatements. To examine retail trading, we follow an approach well established in prior literature: We examine both (1) abnormal retail trading volume and (2) abnormal trade imbalance, which is the proportion of retail trades that are trades to buy shares versus to sell shares. 3 Consistent with retail investors reacting to restatements, we find that retail investors trade more in restatement 3 Similar approaches have been used to examine small trader reactions to events such as earnings announcements (e.g., Bhattacharya 2001; Battalio and Mendenhall 2005; Shanthikumar 2012), analyst recommendations (Malmendier and Shanthikumar 2007; Mikhail, Walther, and Willis 2007; Malmendier and Shanthikumar 2014), and pro-forma earnings announcements (Allee, Bhattacharya, Black, and Christensen 2007; Bhattacharya, Black, Christensen, and Mergenthaler 2007). 3

5 announcement windows than at other times, and trade more in the announcement window for fraud-related restatements than non-fraud restatements. However, retail investors do not sell more strongly for restatements than at other times, nor do they differentiate between fraud and non-fraud restatements in terms of their buy/sell trade imbalance. They also do not sell more strongly, for restatements in general or for fraud-related restatements in particular, during the six-month postannouncement window. These results suggest that retail investors have difficulty interpreting the severity of restatements, and, in particular, differentiating between fraud-related and non-fraud restatements, in the post-sox period we examine. Our results are robust to alternate variable definitions, and the examination of the subset of negative-impact restatements. Retail investors fail to sell more strongly as a percentage of their trade even for restatements that are clearly negative. To gauge whether retail investors are hurt by their failure to sell, we directly examine the returns that follow retail investors announcement-window trades. Retail investors trades for nonfraud restatements are followed by near-zero abnormal returns for up to six months. However retail investors purchases around fraud-related restatement announcements lead to statistically and economically significant negative returns over every horizon examined, significantly more negative than those for non-fraud-restatement purchases. For example, retail investors purchase shares with 42% of their fraud-restatement trades, a similar ratio as for non-fraud (41%). Yet these fraud-related-restatement purchases lead to -8% raw returns (-11.6% abnormal returns) over a three-month horizon. While retail investors avoid some losses with the shares they sell around fraud-related restatements, these results suggest that the failure of retail traders to sell more strongly for fraud-related restatements adversely affects investor welfare, as feared by the SEC. Finally, given growing evidence that dissemination of news by the press aids in the market response to information (e.g., Bushee, Core, Guay, and Hamm 2010; Drake, Guest, and Twedt 4

6 2014; Rogers, Skinner, and Zechman 2016), we examine whether retail investors react more appropriately for restatements with higher levels of press coverage. On one hand, the higher retail trading volumes observed for fraud-related restatements may be a naïve reaction to press coverage, similar to the attention effect buying documented in prior literature (Barber and Odean 2008). On the other hand, press coverage may convey information, facilitate retail investor analysis, and enhance understanding of the restatement, allowing investors to better differentiate between fraudand non-fraud restatements. We examine several press-related variables: an indicator for press coverage, the number of articles covering the restatement, and the salience of the restatement coverage, which is defined by whether the restatement is mentioned in a headline, body, or footnote. We find higher retail trading volume for fraud-related restatements when press coverage is present. In addition, retail investors sell more strongly, as a percentage of their trades, when press coverage of the restatement is higher. We also find some evidence that more salient press coverage is associated with stronger retail investor selling. We do not establish causality, however the evidence from retail investors trading is consistent with high press coverage helping retail investors to understand that they should sell for fraud-related restatements. Even for fraud-related restatements with high press coverage, though, retail investors buy significantly, leading to losses. Overall, our results are consistent with retail investors failing to understand the negative nature of restatements, particularly fraud-related restatements. Note, it is not simply a failure to sell that we observe but significant retail investor buying around fraud-related restatements. It is also important to note that these retail investors do not need to buy to balance institutional investor selling. They make up a small fraction of the market, and are not serving to clear the market. However, we find that retail investors do slightly better for restatements with high press coverage. 5

7 These results are relevant for standard-setters and those interested in individual investor welfare or advising, as they identify a systematic mistake made by retail investors as well as one current mechanism, press coverage, which may help to reduce this mistake. The SEC is making a concerted effort towards improved fraud detection and prevention for the sake of investor welfare (e.g., Shapiro 2011; SEC 2013b; Eaglesham and Rapoport 2015). Our results suggest that clearer disclosure about fraud and irregularities, and broader dissemination of restatement-related news, may be helpful to retail investors when fraud inevitably does occur. In addition, broader questions surrounding the possibility of information overload are becoming increasingly pertinent. 4 Our results indicate that information overload may be a problem for restatements. Our study also contributes to the literature on the market response to restatement- and fraud-related information. We demonstrate that while the market may use some restatementrelated information in a sophisticated way (e.g., Badertscher, Hribar, and Jenkins 2011; Burks 2011; Peterson 2012), retail investors fail to do so. Moreover, our paper contributes to the literature on retail investor trading by examining more recent retail investor trading than prior literature, and examining an event that differs in two ways: It is less common than the events previously examined, but is of greater potential significance. The announcement of a fraud-related restatement would ideally be a clear negative signal to retail investors, but our study shows that it is not. The remainder of the paper is structured as follows. Section 2 discusses related literature and develops hypotheses. Section 3 describes our retail investor trading data and presents results 4 At the 2013 SEC Speaks Conference, SEC Commissioner Troy Paredes summarized the information overload concern in a speech about corporate disclosure. He explained, The information overload concern is that investors will have so much information available to them that they will sometimes be unable to distinguish what is important from what is not. Too frequently, investors get overwhelmed or distracted, misplacing their focus on information that is only marginally useful. The goal of informed investor decision making is not advanced if investors overlook or do not take the time to study valuable information because there is simply too much information to try to engage it constructively. Chair Mary Jo White reiterated this concern months later in a heavily cited speech to the National Association of Corporate Directors (Mary Jo White 2013). 6

8 of a validation test. Section 4 presents descriptive statistics and return results for our restatement sample. Section 5 presents the main results for retail investor trading around restatements, subsequent returns, and the relation between trading and press coverage. Section 6 concludes. 2. Related Literature and Hypothesis Development The dramatic increase in the number of restatements in the early 2000s raises the natural question of whether investors can differentiate between more serious (e.g., fraud) and less serious restatements. Burks (2011) addresses this same general question by examining returns around restatements, focusing primarily on the post-sox period. He finds significantly more negative announcement-window returns for fraud-related restatements, suggesting that at least some portion of the market identifies these restatements as worse than others. But he also finds significantly more negative post-announcement returns in the six and twelve months after the announcement of a fraud-related restatement, suggesting that the market fails to fully incorporate the negative implications of the announcement. While the overall post-restatement drift does not appear worse in the post-sox period than pre-sox, it remains an open question whether retail investors, those the SEC is particularly interested in, are able to react correctly by selling for fraud-related restatements, or whether they continue to hold these stocks with predictably negative returns. Information overload, the failure to process publicly available information, can occur for the market as a whole, as indicated by evidence of stronger market under-reactions to earnings information during periods when investors are more likely to be distracted (DellaVigna and Pollet 2009; Hirshleifer, Lim, and Teoh 2009). But there are reasons to expect retail investors to be particularly affected by potential information overload. Retail investors have less time, investing knowledge, and fewer resources with which to process information than professional investors. Research comparing small investors, who are likely to be retail investors, and large investors, who 7

9 are likely to be institutional investors, has shown a greater failure to process information on the part of small investors. For example, small investors are less likely to use the information in analyst earnings forecasts (Battacharya 2001; Battalio and Mendenhall 2005; Malmendier and Shanthikumar 2014), and are less likely to adjust for analyst conflicts of interest (Malmendier and Shanthikumar 2007; Mikhail, Walther, and Willis 2007). Barber and Odean (2008) show that attention-related buying is stronger among retail investors than institutional investors. On the other hand, small investors often react strongly to visible signals. Malmendier and Shanthikumar (2007) show that small traders sell strongly in response to analyst sell recommendations. Allee, Bhattacharya, Black, and Christensen (2007) and Bhattacharya, Black, Christensen, and Mergenthaler (2007) find that small traders react to pro-forma earnings numbers, particularly when those numbers are placed first in an earnings announcement. Files, Swanson, and Tse (2009) and Huang, Nekrasov, and Teoh (2015) show that the market as a whole reacts more strongly if information is made more salient by disclosure in a headline. There are reasons to expect fraud-related restatements to be one such signal. While fraud is not always disclosed in a headline, fraud-related keywords such as fraud and investigation may be salient to investors. Brazel, Jones, Thayer, and Warne (2015) survey experienced individual investors and find that over half believe that 50% or more of firms commit fraud, and two-thirds believe that fraud risk assessment is important to the investment decision. Retail investors may place similarly high weight on information about fraud. In addition, Barber and Odean (2008) find evidence that the decision to sell a stock is less influenced by limited attention than the decision to buy, since retail investors typically hold a small number of stocks and rarely short-sell. Given that correct fraud-related trading is to sell, it is less likely to be subject to limited-attention effects. 8

10 It is clear that retail traders are at risk for failing to incorporate the important information in a restatement announcement, even if market returns respond. Yet there are reasons to believe that they will sell for fraud-related restatements. Thus, we state our hypotheses in the null form. Our first hypothesis addresses trading volume: H1a. Retail investors do not react to restatements, as measured by higher trading volume. H1b. Retail investors do not react more strongly to fraud-related restatements than non-fraud restatements. Our second hypothesis addresses whether retail investors trade in the correct direction. Given evidence that attention-drawing events are more likely to drive retail investor buying than selling, and given the negative nature of fraud-related restatements, this is a key question. H2a. Retail investor trading is not weighted more heavily towards either buying or selling around restatements than at other times. H2b. Retail investor trading is not weighted more heavily towards either buying or selling for fraud-related restatements than for non-fraud restatements. Finally, given our interest in investor welfare, we conduct additional analyses. First, to understand the return implications of the retail investor trading response, we examine the returns retail investors realize given their trading around restatements. Second, motivated by a growing literature that shows the value of press coverage in improving the overall market response to information (Bushee, Core, Guay, and Hamm 2010; Drake, Guest, and Twedt 2014; Rogers, Skinner, and Zechman 2016), and evidence that the press plays a significant role in uncovering and disseminating information about fraud (Miller 2006; Dyck, Morse, and Zingales 2010), we examine whether press coverage may facilitate a more appropriate retail investor response. 9

11 3. Retail Investor Trading Data Prior research on individual investor trading has largely focused on the 1990s due to data limitations, explained below. In this paper, we utilize a new dataset capturing retail investor trades. In this section, we describe this data and how it compares to some commonly-used datasets in prior literature, and we report results of a test to validate that the data captures overall retail trade. 3.1 Previously-Used Retail/Small/Individual-Investor Trading Data A large body of research on individual investor behavior has analyzed data from a large retail brokerage firm covering (see, e.g., Odean 1998; Barber and Odean 2000; Ivkovic and Weisbenner 2005; Barber and Odean 2008; Hirshleifer, Myers, Myers, and Teoh 2008). This dataset covers almost 80,000 retail brokerage accounts and has a wealth of detailed account-level data. However, because the brokerage dataset is restricted to the early 1990s, it is insufficient to address the question of whether retail investors can differentiate between fraud and non-fraud restatements in the recent era, with its high number of restatements. A second stream of papers has relied on partitioning trades based on trade size (see, e.g., Lee 1992; Battacharya 2001; Shanthikumar 2012), following the approach outlined and tested in Lee and Radhakrishna (2000). Researchers begin with detailed trade and quote data from the NYSE TAQ database. They first determine if the buy- or sell- side of the trade initiates the trade using the Lee and Ready (1991) algorithm. Then, researchers partition the trades into those most likely to have been made by small individual investors, such as trades below a certain dollar value (e.g., $5,000, $10,000), and those most likely to have been made by institutional investors (e.g., those above $50,000) (Lee and Radhakrishna 2000; Odders-White 2000). This approach has the advantage of including all trades made on the exchanges examined; however, this method is primarily effective before the mid-2000s and is unlikely to work in more recent years. 10

12 Institutions began splitting trades much more aggressively in the early 2000s (Malmendier and Shanthikumar 2007). Cready, Kumas, and Subasi (2014) use data on pension fund and mutual fund trading and show that after 2003, and particularly after 2005, transaction sizes are such that the small/large classification is problematic. For example, trade-splitting behavior varies with respect to events of interest, such as earnings announcements. Thus, as Malmendier and Shanthikumar (2007) argue, the trade-size approach is unlikely to be effective after about Data Description We introduce a unique dataset that identifies retail investor trades on the New York Stock Exchange over ten years, from 2004 through Stock exchanges place requirements on order reporting to ensure that key data is consistently reported when orders are submitted. This data includes items such as the number of shares to be traded, whether the order is to buy or sell, etc., but also includes additional information. One of the required data items is the type of investor placing the order. 5 Our dataset exploits this information by collecting data for all trades where at least one side of the trade includes a retail investor. All of the executed retail orders are then aggregated to provide daily totals for each ticker symbol, of the number of trades in which a retail investor purchased shares (buy trades), the number of trades in which a retail investor sold shares (sell trades), and the number of shares bought and sold by retail investors (buy shares and sell shares, respectively). This data has the advantages of identifying whether trades are purchases or sales directly, rather than having to infer this indirectly as with TAQ data, and identifying that the trades are made by retail investors. Thus this dataset addresses the issue of increased trade splitting by institutional investors, which has rendered the small/large method ineffective. While this data 5 NYSE Rule 132(b), and later FINRA Rule 7440, both require reporting of trader type. For example, FINRA Rule 7440 requires orders to include (18) the type of account, i.e., retail, wholesale, employee, proprietary, or any other type of account designated by FINRA, for which the order is submitted. 11

13 does not allow us to examine the behavior of a particular individual as a brokerage account dataset would, it provides ideal data for examining the trading behavior of retail investors as a group. Although our data includes all retail investor trades made on the New York Stock Exchange (NYSE), retail trades that are either routed to alternate exchanges or matched internally by a brokerage house will be excluded from our data. However, because our data captures all retail trades executed on the NYSE, we argue that we are likely to capture a significant portion of retail trade, which allows us to estimate retail investor trading behavior. For the full sample of NYSE common stock from 2004 to 2012, retail trading in our data accounts for 0.94% of total trading volume. For the firms in the final restatement sample, retail investors account for 1.50% of the total trading volume in the three-day window around the restatement announcement. While this may appear low, the percentage of trade captured in our data is similar to Kelley and Tetlock (2008) for the overlapping sample period. 6 We are also unable to obtain data for any other trader group, so lack a benchmark or comparison group with which to compare retail traders. Thus our analyses will more closely mirror those of papers using the Odean (1998) dataset, which focuses on retail investors, than papers using the TAQ-based small/large trader data. Our data is most like that of Kaniel, Saar, and Titman (2008) and Kaniel, Liu, Saar, and Titman (2011); they examine retail investor trading on the NYSE from 2000 through Interestingly, using this data the authors find evidence that retail trades positively predict 6 The percentage of total trading volume that appears as retail trade in our data is 0.94%. This is lower than the percentage reported in Kelley and Tetlock (2008), 2.3%. Their data covers trading during on two major over-the-counter markets. The difference is likely due to two factors. First, their data covers stocks listed on NYSE, AMEX, and Nasdaq, while our data focuses on NYSE. NYSE generally includes larger firms, and retail trade is likely to make up a larger percentage of overall trading volume for smaller firms. For the smallest quintile of firms in our sample, retail trade makes up 2.05% of trading volume. Second, our data includes six years of post-2008 data, when direct retail investing may have dropped (e.g., Browning 2008; Shell 2012). For , retail trade in our data is 2.36% of trading volume. Thus the percentage of trade captured in our data is similar to Kelley and Tetlock (2008). 12

14 subsequent returns. Kelley and Tetlock (2008) find similar results, using retail trades routed to two over-the-counter market centers from 2003 through 2007, and provide suggestive evidence that less sophisticated retail investors may have disproportionately left the market after the negative returns of the early 2000s. These results suggest that retail investors during our sample period may be more sophisticated than small/retail investors examined in prior research for earlier periods. 3.3 Validation We conduct a simple test to validate that our data is likely to proxy for aggregate retail investor trade. Following the methodology of Malmendier and Shanthikumar (2007), we aggregate the trade imbalance of retail traders over each quarter using our data. We then relate this quarterly cumulative trade imbalance to changes in the percentage of shares owned by institutions, as measured using 13-f institutional holdings data from Thomson-Reuters. [Insert Table 1] Table 1 reports the results. TI_SHROUT is defined as the total net shares bought by retail traders over the quarter (Buy_Shares Sell_Shares), normalized by shares outstanding. This captures the percentage of shares outstanding bought (or sold) by retail traders and should capture the extent to which retail ownership of the stock has increased. We would expect retail investor ownership and institutional investor ownership to move in opposite directions. Malmendier and Shanthikumar (2007) report a correlation of between TI_SHARES for small trades and quarterly changes in institutional ownership over the years 1993 through The first column of Table 1, Panel A reports the correlation for the full sample of NYSE firms: with p< The second column reports the correlation for firms that have at least one restatement during the sample period: with p< The magnitudes of these correlations, in comparison to those reported in Malmendier and Shanthikumar (2007, Table 2), suggest that the retail investor trading 13

15 data in our sample is likely to provide as accurate a gauge of quarterly changes in ownership as small-trader data during the earlier period. In Panel B, we present the results of regression analyses in which we cluster standard errors by quarter and firm. The regression model allows us to split trade imbalance (TI) into its buy and sell components. As expected, we find a significantly negative relation between TI_SHROUT and change in institutional ownership in both samples. In addition, the relation between BUY_SHROUT (SELL_SHROUT) and change in institutional ownership are significantly negative (positive) at the 1% level in both samples, and of similar magnitudes. Finally, we estimate the same correlation and regressions restricting to the quarter of the restatement for sample firms. Due to the unbalanced cluster sizes in this sample, we include quarter fixed effects rather than clustering standard errors by quarter. Results are reported in the last two columns of Panels A and B and are similar to the first two samples, suggesting that retail trade imbalances, as measured using our NYSE trade data, capture overall changes in retail investor holdings around restatements. Thus, although the exact amount of trade captured in our dataset is relatively low compared to total volume, it is likely to be a strong proxy for aggregate retail investor trading around our events of interest. 4. Restatement Data We collect data for restatements disclosed from 2004 through 2012, for firms listed on the NYSE, from the Audit Analytics database. Given that prior literature has primarily focused on restatement data through 2005 (e.g., Scholz 2008; Burks 2011), we describe our data in detail, and examine returns around the restatements in our sample to ensure that prior results regarding restatement-related returns extend to our sample. 14

16 4.1 Data Description Audit Analytics identifies restatements made by all SEC registrants to correct accounting practices that do not conform to General Accepted Accounting Principles (GAAP). Hence, the sample excludes retrospective revisions for comparative purposes, retrospective application of accounting principles, and changes in presentation as a result of mergers and acquisitions. We require the firms to have non-missing CRSP and COMPUSTAT basic data in the year of restatement. Table 2 describes the sample selection. [Insert Table 2] Audit Analytics provides an initial filing date (FILE_DATE_NUM); however, this date can be later than the date of initial restatement announcement. To identify the first announcement mentioning the upcoming restatement, we manually search for press releases or articles related to each restatement in Factiva and use the first announcement date as the initial announcement date of the restatement. For 112 of the 660 restatements in our final sample, we find an earlier announcement date than the disclosure date reported in Audit Analytics, with a mean (median) gap of 24 (seven) days between our date and the date from Audit Analytics. Starting with 1314 NYSE restatements, we exclude restatements in which firms amend financial reports due to changes in corporate internal structure (92 observations), restatements without restated past filings but with only updated comparable-period information in future filings (150 observations), those for foreign issuers and quasi-government entities (134 observations), and restatements due to changes in accounting estimates and policies (8 observations). In cases of multiple restatements within a year, we keep the first restatement and eliminate all following restatements (155 observations). Finally, we eliminate restatements without retail trading data (17 15

17 observations) or other data required for the analysis (97 observations). This leaves us with a sample of 660 restatements. [Insert Table 3] Table 3 describes the distribution of restatements over time as well as restatement characteristics. The number of restatements peaks at 187 in Our sample period includes a dip in restatements during as well as a second rise in frequency in 2011 and We also see variation in the percentage of restatements related to fraud. In total, 14.7% of the restatements in our sample are associated with fraud. The frequency of fraud-related restatements is highest in 2004 (23%) and lowest in 2010 (2.8%), with only one fraud-related restatement. Other restatement characteristics show variation over time, but with few notable trends or outliers, other than a particularly high number of operating-lease-related restatements in Returns around Restatement Announcements Prior research has documented a more negative initial reaction and more negative postannouncement returns for fraud-related restatements, even in the post-sox era (Scholz 2008; Burks 2011). However, our sample extends seven years beyond that examined in either study, we focus on NYSE firms rather than all publicly traded firms, and we begin with Audit Analytics data rather than GAO data (allowing us to extend the sample period). Thus, before examining retail investor responses to restatements, we examine returns for our sample. We use the following model to assess whether market-wide returns are more negative for fraudulent restatements, BHAR[X, Y] i = α + β 1 FRAUD i + β 2 Restatement Characteristics i + β 3 General Controls i + ε i, (1) where BHAR[X,Y] is the buy-and-hold abnormal return over the trading-day window [X,Y] relative to the restatement announcement date. The variable of interest is FRAUD, an indicator variable 16

18 equal to 1 if the restatement is described in Audit Analytics as accounting fraud or as having related SEC investigations. 7 These restatements involve suspected or confirmed intentional manipulation, as opposed to technical errors. We classify the remaining restatements as non-fraud restatements. We predict that the coefficient on FRAUD, β 1, is negative, consistent with prior literature, due to the more serious nature of fraud-related restatements. 8 Our primary focus is on whether FRAUD restatements earn more negative returns, and whether investors react more strongly and more negatively to them. As such, for all of our primary analyses, we first estimate the model with few controls, then with a set of control variables for other potential drivers of announcement-window returns and trading, and finally with an additional set of restatement characteristics to determine if any differential reactions we see related to fraud are in fact more subtle e.g., related to the fact that fraud-restatement announcements are less likely to include an estimate for the magnitude of the eventual restatement. We measure abnormal returns using buy-and-hold, characteristic-adjusted returns. Following the application of Daniel, Grinblatt, Titman, and Wermers (1997) used in Burks (2011), we form benchmark portfolios by partitioning all COMPUSTAT/CRSP NYSE firms into size deciles based on market value of common equity at the end of each June, and then sorting each size decile into book-to-market quintiles based on industry-adjusted book-to-market at the end of December before the size assignment, creating 50 benchmark portfolios. Note that while we do 7 Hennes, Leone, and Miller (2008) provide an irregularity/error classification for restatements in the GAO database. We rely on Audit Analytics rather than Hennes, Leone, and Miller s (2008) classification to identify fraudulent restatements due to our different data source and sample period. Badertscher, Hribar, and Jenkins (2011) report a 94 percent correlation between the two classifications for the overlapping sample. 8 Palmrose, Richardson, and Scholz (2004); Scholz (2008); and Burks (2011) find more negative announcement-window returns for fraud-related restatements than non-fraud restatements. Regarding postannouncement returns: Palmrose, Richardson, and Scholz (2004) do not examine long-run post-announcement returns. Burks (2011) finds more negative post-announcement returns for fraud-related restatements than non-fraud. Scholz (2008) finds that restatements with more negative announcement-window returns also earn more negative subsequent returns over the following year, but that fraud does not have an incremental impact above and beyond this effect. 17

19 not include momentum in our matching, we include returns in the six months prior to the restatement as a control variable in our regressions. We subtract the benchmark portfolio s equally weighted buy-and-hold return from the restatement firm s buy-and-hold return to compute the abnormal buy-and-hold return. We calculate size-adjusted announcement window abnormal returns in the three days around the restatement announcement, BHAR_ANNOUNCE[-1,+1] as well as size- and book-to-market-adjusted long-run abnormal buy-and-hold returns over two sixmonth periods relative to the announcement date: BHAR[+2,+126] and BHAR[+127, +252]. 9 The set of control variables, General Controls, relates to general factors that potentially affect returns around the restatement announcement, and includes firm size (SIZE), book-to-market ratio (BM), abnormal returns in the six months preceding the announcement (RETURN_PRIOR), whether earnings are announced concurrently during the restatement announcement window (EA), and the magnitude of the earnings surprise if earnings are announced (ESUP). The list of possible restatement characteristics we could include is extensive. However, as Table 4, Panel C, shows, the correlations among these variables are very high. To avoid multicollinearity and aid in interpretation of results, we focus on a few restatement characteristics that we believe are most likely to underlie any differential returns and trading responses for fraud 9 Given that our focus is on investor trading at and around the restatement announcement, and the returns that follow, we focus on the traditional announcement-date-related windows. However following Burks (2011), for completeness, we also calculate returns over windows defined around the episode window that begins with the initial announcement and ends with the announcing of the full earnings impact of the restatement (untabulated). These windows are labeled as BHAR_EPISODE[-1,+1], BHAR_POST_EPISODE[+2,+126], and BHAR_POST_EPISODE[+127, +252]. The coefficient on FRAUD in Equation (1) is significantly negative at the 1% level or better, with magnitudes ranging from to , for BHAR_EPISODE[-1,+1]. The coefficient for BHAR_POST_EPISODE[+2,+126] is significantly negative in the model with no additional control variables beyond the year fixed effects, significantly negative in the model with general controls, and statistically insignificant in the model including other restatement characteristics. The coefficients on FRAUD are all statistically insignificant for BHAR_POST_EPISODE[+127, +252]), as with BHAR[+127,+252]. Overall, this suggests that, not surprisingly, some of the post-announcement negative returns for fraud-related restatements occur in the episode window, and is consistent with the findings of Burks (2011). 18

20 restatements. 10 First, we include whether the restatement is prompted by the SEC (SEC_PROMPTS) as SEC-prompted restatements are often associated with fraud (correlation of 0.438), and many of these are highly visible. Second, we control for the magnitude of the restatement s cumulative impact on earnings (MAG), and whether the initial announcement fails to include the earnings impact of the restatement (NO_INITIAL_MAG) as each of these is shown to be significantly related to announcement-window returns in both Palmrose, Richardson, and Scholz (2004) and Burks (2011). 11 Individually, we would expect SEC_PROMPTS to be associated with more negative returns, MAG to be positively associated with returns, and NO_INITIAL_MAG to be negatively associated with returns. However, given the correlations among the characteristics, and with FRAUD, it is unclear what to expect for each variable when included together. Our focus, however, is not on the coefficient estimates for these variables, but rather on whether they explain any differential returns (or trading) found for FRAUD, i.e., we look at what happens to the coefficient estimate for FRAUD in the model with these other characteristics included. [Insert Table 4] Table 4, Panels A and B, present summary statistics for returns around restatement announcements, for the full sample and partitioned based on whether the restatement is related to fraud. In all three cases, abnormal returns in the month prior to the restatement are insignificant. However, the returns in the three trading-day window surrounding the announcement are 10 Our regression results for differential returns and trading around fraud-related restatements (Tables 5 and 7) are quantitatively similar when the full set of restatement characteristics and general controls listed in Table 4 are included as control variables in the regression (untabulated). Results for the additional variables are generally statistically insignificant. The primary exception is POS_AA, an indicator for MAG>0. When included together with MAG, coefficient estimates on the two variables are of opposite sign and sometimes statistically significant. 11 Each paper includes a broad set of restatement characteristics when examining determinants of announcement-window returns and finds several that are statistically significant (Palmrose, Richardson, and Schultz 2004 Table 5; Burks 2011 Table 3). However, only these two characteristics are found to be significant in both studies. 19

21 significantly negative, at -0.9% for non-fraud restatements and -3.8% for fraud-related restatements. Post-announcement returns are negative or insignificant for the two windows we examine for the pooled sample, but non-fraud restatements are followed by insignificant 1.0% returns in the subsequent six months, while fraud-related restatements are followed by -8.7%, significant at the 1% level. The difference between the two is significant, with p= Thus the univariate statistics indicate more negative announcement-window and post-announcement returns for fraud-related restatements than non-fraud restatements, with statistically and economically significant differences between the two. [Insert Table 5] Table 5 presents the results of estimating Equation 1. As indicated in Table 4, Panel C, many of the correlations between FRAUD and other restatement characteristics are large and significant. We estimate the model first without controls, second with controls for variables that might affect returns, and finally with additional restatement characteristics. The first three columns present results for announcement-window returns. Note, while fixed effects are included we report the intercept as estimated using all observations, for interpretability, throughout the paper. The fixed effect coefficients thus capture deviations from this mean and average to zero across the sample. The average announcement-window return for restatement announcements is negative before controlling for firm characteristics and concurrent earnings information, consistent with summary statistics (Intercept, -0.9%), but insignificant when these controls are included. Announcement-window returns are significantly more negative for fraud-related restatements (coefficient on FRAUD). Fraud-related restatements earn additional negative returns ranging from -2.9% to -3.4% depending on the specification. This is consistent with Palmrose, Richardson, and 20

22 Scholz (2004), Scholz (2008), and Burks (2011), and reinforces that fraud-related restatements are more negative than non-fraud restatements. Columns 4-6 (7-9) report results for the six months following the announcement window (months seven through twelve). The insignificant estimates on the intercept in columns 4-6, 8, and 9 suggest that there is no sustained drift for the average restatement announcement; however, we find significantly negative coefficients on FRAUD for the [+2,+126] window in all three specifications, suggesting that fraud-related restatements are followed by predictably negative returns relative to size- and book-to-market benchmark firms. The coefficients are large, with sixmonth incremental negative returns ranging from -8% to -9.7% for fraud-related restatements versus other restatements. We do not find continued drift in the subsequent six months. 12 The results reported in this section verify that fraud-related restatements are associated with more negative returns in the announcement window and subsequent six months. Prior results extend to our sample. This suggests that if retail investors fail to sell following fraud-related restatements, they are likely to earn more negative returns. In the remainder of the paper, we examine the retail investor response to these restatements. 5. Empirical Methodology and Results The main focus of our analysis is on retail investor trading. We assess retail investors reactions in terms of the volume of trading and the direction (buying vs. selling) of the trading reaction. In this section, we describe our methodology and report results for retail investors trading around announcements, subsequent returns, and variation with respect to press coverage. 12 Given that prior literature has not examined returns after 2005, we also estimate Equation 1 for the subsample (408 observations) in untabulated analyses. We find that fraud-related restatements earn an incremental -2.6% to -3.4% abnormal return in the [-1,+1] window around the restatement, and are followed by an incremental -12.7% to -14.2% abnormal return over the subsequent six months. Thus the incremental negative announcement-window and post-announcement returns persist past

23 5.1 Retail Investor Trading Around Restatement Announcements Our analysis focuses on two measures abnormal trading volume and abnormal trade imbalance. To measure retail trading volume, we first calculate the raw total number of retail trades for firm i on day t as the sum of buy and sell trades, TOT_TRADES Raw i. We then normalize this measure by subtracting the mean TOT_TRADES Raw i and dividing by the standard deviation of TOT_TRADES Raw i, measured over trading days [-252, -31] relative to the initial restatement announcement, similar to Malmendier and Shanthikumar (2007, 2014) and Shanthikumar (2012). Thus, the abnormal total trades is defined as TOT_TRADES i,t = TOT_TRADES i,t Raw Raw mean(tot_trades i,[ 252, 31] ) Raw. (2) std(tot_trades i,[ 252, 31] ) The normalized measure captures abnormal retail volume around firm i s restatement announcement adjusted for how retail investors normally trade firm i during a pre-announcement window. If trading around the restatement announcement follows the same distribution as during the pre-announcement window, then the distribution of TOT_TRADES should have mean zero and standard deviation one. The normalization allows us to compare retail trading behavior over time and across firms. We also compute an alternative measure of abnormal retail volume using the number of shares traded (TOT_SHARESi,t ). It may be that more investors are trading, which is likely to appear in both more trades and more shares traded, or it may be that those investors who are trading are making larger trades, which would appear only in an increase in number of shares. Thus we report results for both throughout the paper The primary alternate normalization approach used in the literature (see, in particular, Allee, Bhattacharya, Black, and Christensen 2007; Bhattacharya, Black, Christensen, and Mergenthaler 2007; and Mikhail, Walther, and Willis 2007) is to normalize by the mean, rather than the standard deviation, and to calculate trade imbalance as net trades minus mean net trades normalized by mean total trading volume. We calculate these alternatives as well, and replicate the trade-related tests (Tables 7 and 9) using the alternative measures. Results are qualitatively similar. 22