Founder Replacement and Startup Performance

Founder Replacement and Startup Performance Abstract We provide causal evidence that venture capitalists (VCs) improve the performance of their portfolio companies by replacing founders. Using a database of venture capital financings augmented with hand-collected founder turnover events, we exploit shocks to the supply of outside executives via 14 states’ changes to non-compete laws from 1995 to 2016. Naive regressions of startup performance on replacement suggest a negative correlation that may reflect negative selection. Indeed, instrumented regressions reverse the sign of this effect, suggesting that founder replacement instead improves performance. The evidence points to the replacement of founders as a specific mechanism by which VCs add value. Received January 16, 2016; editorial decision August 3, 2017 by Editor Francesca Cornelli. Authors have furnished an Internet Appendix, which is available on the Oxford University Press Web Site next to the link to the final published paper online. It is well accepted that venture capital (VC) is a “hits” business. In a sample of over 22,000 VC-funded startups founded between 1987 and 2008, 75% had a liquidation value of zero while 0.39% had an exit value of $500 million or greater (Hall and Woodward 2010). Research indicates that returns are enhanced by investor skills, which one might group by (1) initial selection of investment targets and (2) post-investment intervention.1 Recently, scholars have turned their attention to the question of whether post-investment intervention by “activist” investors truly improves outcomes for portfolio companies (Bottazzi, Da Rin, and Hellmann 2008). Chemmanur, Krishnan, and Nancy (2011) use restricted-access Census data to show that startups ineligible for Small Business Administration support achieve greater total factor productivity after raising VC, suggesting that investors provide more than just capital. Bernstein, Giroud, and Townsend (2016) similarly find that VC-backed firms are more likely to achieve liquidity events once their investors are able to visit via a nonstop flight. But neither paper identifies specific actions undertaken by investors, leaving open the question of exactly how activist investors add value. Gorman and Sahlman (1986) list three nonfinancial areas, where investors spend time ostensibly in the interest of improving performance. First, VCs assist with strategic and operational planning. In support of the notion that investors influence strategic direction, Hsu (2006) finds that VC-backed ventures are more likely to adopt cooperative commercialization strategies. But whether such assistance improves outcomes remains in question, especially as Kaplan, Sensoy, and Strömberg (2009) see little change in business plans among VC-backed startups that achieve initial public offerings (IPOs). Second, investors may make introductions to customers that facilitate sales and drive revenue growth. The plausibility of this mechanism is underscored by Chemmanur, Krishnan, and Nancy (2011), who suggest that TFP gains for VC-backed startups are largely coincident with increased sales. But customer introductions are difficult to observe empirically, so constructing a clean test of this mechanism is difficult. The third category—recruiting managers—is easier to observe; indeed, VCs are known to play a role in recruiting (see Amornsiripanitch, Gompers, and Xuan 2015). Nevertheless, it is not straightforward to conclude a direct link between such actions and performance. Recruiting can be purely additive, such as when an investor brings a vice president of marketing to an early-stage company that previously did not have one, or it can involve replacing existing personnel. For example, the relevant survey question in Bottazzi, Da Rin, and Hellmann (2008) asks, “Has your firm been involved in recruiting senior management for this company?” which could be of either type. Additive recruiting is unlikely to be controversial whereas founders may resist being replaced. At least four studies have examined founder replacement. In a survey of 170 Silicon Valley based startups, Hellmann and Puri (2002) find that VC-backed ventures are more likely than others to replace the original founder-CEO (and execute such replacements earlier in the life of a startup). They attribute founder replacement to a process of “professionalization” whereby the adolescent venture becomes a more mature company. Consistent with this view, and also using survey data from approximately 200 (nationwide) companies, Wasserman (2003) finds that founder replacement coincides with milestones in the development of a startup such as completing product development or raising a new round of financing. Wasserman also finds that the likelihood of a founder being replaced is increasing in the number of outsiders on the board of directors, suggesting that investors may replace founders proactively. Kaplan, Sensoy, and Strömberg (2009) find that 42% of founders among 50 VC-backed startups that completed an IPO were replaced, suggesting that such “professionalization” may be associated with positive venture outcomes. Although these studies provide a wealth of insight into the phenomenon of founder replacement, including reasons for replacement and the subsequent disposition of the replaced founder, they do not formally test the connection between founder replacement and venture outcomes. Chen and Thompson (2015) attempt to draw a connection between founder replacement and performance by merging the Danish register of 4,172 of new businesses with the country’s register data. They note that startups experiencing founder replacement were more likely to fail, although firms that had a replacement and nonetheless survived grew faster. However, they stop short of making causal claims. Drawing inferences regarding the impact of founder replacement on performance is challenging because founder replacement is endogenous. Founders may decide to leave the firm voluntarily, either because they see their startup’s prospects as dim or because they are “serial” entrepreneurs who prefer to be involved only in the early stages and then depart to start another venture. Replacement may instead be involuntary. Control rights afforded investors via contracts as well as voting rights on the board of directors enable investors to force founders to relinquish their role. They may replace a founder when the business is struggling—as Chen and Thompson’s (2015) data suggest—but they may also elect to replace when the startup is growing quickly yet the investors doubt the founder’s ability to scale up the company (as Wasserman 2003 suggests). In addition, the quality of the person hired to replace the founder may be endogenous. It may be harder to attract strong executives to struggling startups. Moreover, the ability to attract top talent may depend on the quality of the investors and their networks (Amornsiripanitch, Gompers, and Xuan 2015). It might seem self-evident that replacing founders would help firm performance. If investors are rational and add value by monitoring the firm (Bottazzi, Da Rin, and Hellmann 2008; Chemmanur, Krishnan, and Nancy 2011; Bernstein, Giroud, and Townsend 2016), then they should not replace founders unless doing so is beneficial. However, if investors think that they are better informed than the founders but are often incorrect, replacement could be generally detrimental. For example, investors may underestimate the influence of a founder and thus the negative impact of their departure. Moreover, even if investors are correct that the founder should leave the company, removing a founder may have unintended negative consequences such as if loyal-to-the-founder employees become disenchanted and leave. (They may even be recruited away by the deposed founder.) Investors sensitive to that risk may instead try to retain the replaced founder in a different role, but the founder may thwart this plan by refusing to stay once replaced. To address the issue of the effect of founder replacement on firm outcomes, we construct a novel database of VC-backed founders and their replacements. The data builds on the VentureSource repository of entrepreneurial firms, financings, investors and executives. A multi-pronged data collection and cleaning augmented VentureSource by identifying founders as well as replacements of founders (in executive roles, i.e., VP and above) at VC-backed firms founded between 1995 and 2008. Our final sample includes 11,929 firms and 19,830 founders. Some 15% of firms have at least one founder replacement in our sample period, almost 40% of whom appear to stay at the startup after they are replaced. The first major question that we ask is whether these replacements correlate with startup firm exit outcomes. Naive regressions show a negative correlation between founder replacement and liquidity events. Similar to Wasserman (2003), we find that founder replacement is more likely to occur following a new round of financing as well as when the board contains more investors. But as argued above, even if VCs play a primary role in replacing founders the negative correlation between replacement and subsequent performance could be explained by selection if investors choose to replace a founder when a startup is in trouble or because a highly qualified replacement is hard to find (including when founders relinquish their role voluntarily). We then instrument for founder replacement using a plausibly exogenous shock to the supply of executives who might serve as suitable replacements: changes in the enforceability of employee non-compete agreements. Non-compete agreements have frequently been shown to restrict the mobility of workers, especially technologists and executives in the sorts of high-potential industries VCs tend to invest in (Marx, Strumsky, and Fleming 2009; Marx 2011; Garmaise 2011). Thus the ability of an investor to attract a qualified replacement may depend on the extent to which non-compete agreements are enforceable. The large-scale data on founder replacement we build off of VentureSource enables us to assess the impact of non-compete agreements by exploiting staggered changes in 14 states, some of which tightened enforceability while others loosened enforceability. Founders are less (more) likely to be replaced when non-compete enforceability has been strengthened (weakened). The larger data set of founder replacements we collected enables us to test the effect of these employment contracts on replacement rates and subsequent venture performance. Instrumenting for founder replacement with these policy changes shows that replacement increases the likelihood of achieving a high-quality liquidity event such as an IPO or attractive acquisition. The instrumented finding reverses the correlation found in the naive cross-sectional analysis. Decomposition of the instrumented results reveals which types of replacements have the greatest impact. Replacing founders who hold CXO roles, such as Chief Executive Officer (CEO) and Chief Financial Officer (CFO), is more consequential than replacing founders in lower roles. Interestingly, replacement appears to help more when replaced founders leave the startup after relinquishing their role. Taken together, these findings point to the role of venture capitalists in professionalizing their portfolio companies by replacing founders with more experienced executives. Replacement is more common following a round of funding and when investors hold more board power, and replacement contributes more to positive venture outcomes when CXO-level founders leave the company. Insofar as venture capitalists play an important role in both the decision to replace founders and identify their replacements, the positive causal effects we find establish a mechanism by which VCs add value to their portfolio firms. In doing so, we extend the literature on how venture capitalists add value, which has previously demonstrated some causal effect of VC activism on performance but has left open the question of how this value is added. 1. Data The objective of the data collection discussed here and in more detail in the Online Appendix is to create a representative sample of VC-backed founders and the incidence of their replacement. To our knowledge, such a database with broad coverage does not exist, so we assembled one using several different sources of information. To start, we collected the set of VC-backed startups founded from 1995 to 2008 using VentureSource. VentureSource is a database of venture capital transactions, entrepreneurial firms, company executives, investments and outcomes provided by Dow Jones.2 VentureSource is however less reliable in capturing information about founders as startups are not required to report exhaustive founder data. Rather, VentureSource gathers information on founders from the startups themselves as well as third-party sources. We addressed these limitations with several data collection efforts. VentureSource has incomplete coverage of founders either because some firms have no founders identified or similarly, some of the executives of the firm are incorrectly labeled as nonfounders. We addressed these issues by starting with the data from Ewens and Fons-Rosen 2015 firms along with an extensive search for missing founders using LinkedIn, Crunchbase, company Web sites, and CapitalIQ. For the 2,159 firms in which VentureSource listed no founders, we found 3,516 missing founders. Next, even if a startup has one founder it may be that other executives listed in VentureSource for that firm are missing the founder label. To begin, for all 6,219 firms with just one founder, a research assistant examined all the other executives using the Web sites mentioned above to determine whether that executive was also a founder. This process resulted in 1,226 additional founders. Several other data collection tasks were completed to try and remedy missing founders (the Online Appendix details each of these in depth). Using the steps above we found 5,259 additional founders, which raised the average founding team size from 1.6 in the raw VentureSource data to 2.15 in our final sample. This compares favorably with prior work on founding teams. Kaplan, Sensoy, and Strömberg 2009 report 1.9 founders on average in their same of 48 venture-backed companies that completed an IPO. Beckman 2006 extend the data set used by Hellmann and Puri 2002 to include all founders of the 173 Silicon-Valley-based companies collected by Burton 1995, finding 2.2 founders on average. Wasserman 2003 reports an average of 2.5 founders among a combination of 202 venture-backed and non-venture-backed startups. With the new founders collected, sample creation begins with the the set of all VC-backed entrepreneurial firms founded between 1995 and 2008. The lower bound of founding year ensures that we can collect information about replacements via all the sources discussed below, while the upper bound ensures that we have time for exits as the sample ends in April 2017. We further filter VentureSource data according to its coverage of management teams by requiring that the firm has at least one founder (90% of firms have at least one after data cleaning) and raised some capital from a traditional venture capital firm.3 We also require that the founder have a title at or above the level of vice president to ensure they have a major operating role at the firm. The final sample has 19,830 founders of 11,929 entrepreneurial firms. Over 75% of the firms in the sample have exited by April of 2017.4Table 1 provides a summary of most of the variables used in this paper, and Table 2 provides summary statistics. Table 1 Variable description Went public  Startup completed initial public offering by end of sample (April 2017)  Acquired  Startup exited via an acquisition or merger by the end of sample with valuation at least 125% of total capital raised (April 2017). If unknown, exit value is assumed to be 25% of capital invested  Log exit value  Ln price of acquisition or merger  IPO/Acq.  Startup exited via an IPO or an acquisition. If unknown, exit value is assumed to be 25% of capital invested  Still private  Startup remains private as of the end of the sample (April 2017)  Out of business  Startup went out of business by the end of the sample (April 2017)  Year firm founded  Startup founding year, set to the year of first VC financing if unknown  Biotech  Startup industry is health care or biotechnology  Information technology  Startup industry is information technology  Year first VC  Year the startup first raised equity capital from VCs  First capital raised  Capital raised in the first first round of VC financing  Total capital raised (m)  Total capital raised by a startup across all its financing events  Capital stock  Capital raised as of each financing event  Total equity financings (all)  Total financing rounds with VC for the startup  Size of VC board  Number of board member investors as of each financing event  Age of firm  Age of entrepreneurial firm at a financing event in years since firm founding  CXO  Dummy for each of the major titles for executives: (where “X” can be E, F, T, I, or M)  Solo founder  Founder is only executive at the startup at the time of founding  Syndicate size  The number of investors in the current financing round  Profitable at financing  Startup reported profits in a given financing  Increased Enforceability  An indicator for whether a startup was in a state that had a decrease ($$-1$$) or an increase (1) in non-compete enforceability, and (0) represents no change  Founder replaced  Two executives at the startup had the same nonshared job title, and one joined later than the founding date.  Stayed  Replaced founder stayed with the company instead of leaving  Round # FEs  Financing round number fixed effects  Industry FEs  Startup industry fixed effects: “Business/Consumer/Retail,” “Healthcare,” “Information Technology” and “Other”  State FEs  State fixed effects for the headquarters of the startup  Year FEs  Financing year fixed effects  Went public  Startup completed initial public offering by end of sample (April 2017)  Acquired  Startup exited via an acquisition or merger by the end of sample with valuation at least 125% of total capital raised (April 2017). If unknown, exit value is assumed to be 25% of capital invested  Log exit value  Ln price of acquisition or merger  IPO/Acq.  Startup exited via an IPO or an acquisition. If unknown, exit value is assumed to be 25% of capital invested  Still private  Startup remains private as of the end of the sample (April 2017)  Out of business  Startup went out of business by the end of the sample (April 2017)  Year firm founded  Startup founding year, set to the year of first VC financing if unknown  Biotech  Startup industry is health care or biotechnology  Information technology  Startup industry is information technology  Year first VC  Year the startup first raised equity capital from VCs  First capital raised  Capital raised in the first first round of VC financing  Total capital raised (m)  Total capital raised by a startup across all its financing events  Capital stock  Capital raised as of each financing event  Total equity financings (all)  Total financing rounds with VC for the startup  Size of VC board  Number of board member investors as of each financing event  Age of firm  Age of entrepreneurial firm at a financing event in years since firm founding  CXO  Dummy for each of the major titles for executives: (where “X” can be E, F, T, I, or M)  Solo founder  Founder is only executive at the startup at the time of founding  Syndicate size  The number of investors in the current financing round  Profitable at financing  Startup reported profits in a given financing  Increased Enforceability  An indicator for whether a startup was in a state that had a decrease ($$-1$$) or an increase (1) in non-compete enforceability, and (0) represents no change  Founder replaced  Two executives at the startup had the same nonshared job title, and one joined later than the founding date.  Stayed  Replaced founder stayed with the company instead of leaving  Round # FEs  Financing round number fixed effects  Industry FEs  Startup industry fixed effects: “Business/Consumer/Retail,” “Healthcare,” “Information Technology” and “Other”  State FEs  State fixed effects for the headquarters of the startup  Year FEs  Financing year fixed effects  The table reports descriptions of the variables used in regression analysis. Table 2 Summary statistics    Firm characteristics     Mean  SD  Min  p25  p50  p75  Max  Firms  Acquired  0.41  0.49  0  0  0  1  1  11929  Went public  0.060  0.24  0  0  0  0  1  11929  Out of business  0.28  0.45  0  0  0  1  1  11929  Still private  0.24  0.43  0  0  0  0  1  11929  First capital raised  6.47  20.1  0.0100  1.50  3.50  6.75  1500  11929  Year firm founded  2001.0  3.82  1990  1998  2000  2004  2010  11929  Information technology  0.54  0.50  0  0  1  1  1  11929  Biotech  0.18  0.39  0  0  0  0  1  11929  California HQ  0.41  0.49  0  0  0  1  1  11929  Texas HQ  0.053  0.22  0  0  0  0  1  11929  New York HQ  0.066  0.25  0  0  0  0  1  11929  Total equity financings (all)  3.53  2.39  1  2  3  5  24  11929  Total capital raised (m)  37.6  126.4  0  5.35  16  40.8  10328.6  11929  Year first VC  2002.5  4.29  1995  1999  2001  2006  2014  11929  Founder replaced?  0.15  0.36  0  0  0  0  1  11929     Firm characteristics     Mean  SD  Min  p25  p50  p75  Max  Firms  Acquired  0.41  0.49  0  0  0  1  1  11929  Went public  0.060  0.24  0  0  0  0  1  11929  Out of business  0.28  0.45  0  0  0  1  1  11929  Still private  0.24  0.43  0  0  0  0  1  11929  First capital raised  6.47  20.1  0.0100  1.50  3.50  6.75  1500  11929  Year firm founded  2001.0  3.82  1990  1998  2000  2004  2010  11929  Information technology  0.54  0.50  0  0  1  1  1  11929  Biotech  0.18  0.39  0  0  0  0  1  11929  California HQ  0.41  0.49  0  0  0  1  1  11929  Texas HQ  0.053  0.22  0  0  0  0  1  11929  New York HQ  0.066  0.25  0  0  0  0  1  11929  Total equity financings (all)  3.53  2.39  1  2  3  5  24  11929  Total capital raised (m)  37.6  126.4  0  5.35  16  40.8  10328.6  11929  Year first VC  2002.5  4.29  1995  1999  2001  2006  2014  11929  Founder replaced?  0.15  0.36  0  0  0  0  1  11929  The table reports the summary statistics of the firms in the sample. 1.1 Identifying founder replacement Recruiting executives are one of the most commonly mentioned value-add activities observed in the literature on VC monitoring (Gorman and Sahlman 1986; Hellmann and Puri 2002; Bottazzi, Da Rin, and Hellmann 2008). Recruiting could be “additive” in that it helps to complete a nascent founding team, for example, by adding a Vice President of Marketing to a technology-focused startup. But recruiting can also take place for roles already occupied when a replacement is sought. Additive recruiting is unlikely to be controversial, whereas our interest is in the dynamics and impact of replacement. Replacement might be uncontroversial if founders are eager to relinquish their role, or it might be difficult if founders and investors differ in their view of the founders’ suitability to continue in their current role. VentureSource includes information on top-level managers, executives and investor board members. For each executive, VentureSource contains the title held at the venture-backed firm(s) where that person worked. Whenever we observe two individuals at a startup with the same title (excepting inherently joint titles such as “co-CEO”) we conclude that a replacement has occurred. We normalize job titles both by level (e.g., “VP” and “Vice President”) and by function (e.g., “Software Development” vs. “Software Engineering”), while being careful not to lump together titles at the same level and in the same function that are nonetheless distinct (e.g., “VP North American Sales” and “VP International Sales”). Since we aim to identify within-firm replacements, most of the within-firm variation in title naming is due to typography. Because we are ultimately interested in the dynamics of founder replacement, the join date for each new occupant of a given title is essential.5 Unfortunately, join dates are missing for approximately 70% of the replacement executives in VentureSource. We undertook a data collection process using company Web sites, Capital IQ, Zoominfo and public LinkedIn resumes, which typically include an online biography or resume from which the join date can be extracted or inferred. The comparison of titles across all executives identifies a potential replacement. With this list in hand, we have a smaller set of individuals for which to search for join dates. We are able to add the join date for more than 1,500 replacement executives, reducing the missing join dates to 16% of replacement executives. Founders who were replaced but for whom we do not have the join date of the executive who replaced them are dropped from the analysis as we cannot properly establish the timing of the replacement.6 For nonjoint titles for which we have join dates for all occupants, we take the join date(s) of the nonfounder occupant(s) as an indication of a founder replacement. For example, if a startup had both a founder and a nonfounder with the job titles “VP Product” and “Vice President of Product Management” with start dates of January 1, 1995 and June 5, 1997, we take June 5, 1997, as the date of the replacement. We then retain the set of these replacements where the first to hold the position was a founder of the company. One additional concern regarding our sample construction is that the firms that are out of the sample either failed or were shut down before VentureSource collected the data on replacement. Similarly, people who were associated with the company may not have made that known online. Such selection will attenuate any negative relationship between replacement and firm performance. For the question of whether replacement matters, we may have too many “good” replacements (i.e., those that are worth it and those that help). We researched twenty-five random out-of-sample firms to isolate any patterns. Sixteen of the companies appear to have failed and have not raised new VC in many years. Several of the remaining are in nontraditional VC industries such as retail and restaurants where VentureSource may have poor coverage. Overall, the sample of entrepreneurial firms for which we are confident about replacement events is representative of the typical VC-backed firm over the sample period. 1.1.1 Decomposing the nature of replacement As characteristics of the replaced founder, the incoming executive, or the replacement more generally may affect subsequent performance, we collect additional data regarding replaced founders and their incoming replacements. The above-described data collection tells us the role held by the replaced founder, and VentureSource contains a “biography string” listing previous positions. The string does not indicate the years of experience the replacement had, whether s/he had previously founded a startup, or anything regarding educational background. We also want to know what happened to the founder following that replacement as well as characteristics of the incoming executive. Using LinkedIn, we were able to capture career histories for 1,322 of the 1,999 replaced founders as well as the new, incoming managers who replaced them (a total of 2,028 executives).7 In their detailed survey data, Hellmann and Puri (2002) find that 40% of replaced founders continue at a startup in a new role, which they refer to as an “accommodating” replacement as opposed to a “separating” replacement where the replaced founder leaves the company. We classify replacements into these two categories as follows: If VentureSource lists a subsequent job for that founder at the startup, we label the replacement as “accommodating.” Even if VentureSource does not show a subsequent role for the replaced founder, we label the replacement as “accommodating” if their LinkedIn profile claims that they were employed by the firm for at least two years after the replacement date in VentureSource. This condition holds unless LinkedIn lists another job within that two-year period (in case the founder moved to an advisory role or such). The Online Appendix provides additional detail on this aspect of the data collection process. We find 38% of replacements to have been “accommodating,” rather close to the 40% reported in Hellmann and Puri (2002). Replaced founders who stay have less experience than those who leave but are more likely to have previously founded a company. They also appear somewhat more likely to have a PhD and somewhat less likely to have an MBA (Table A2 in the Online Appendix). Our analysis thus builds on Hellmann and Puri 2002 in that we are able to assess the causal effect of different types of replacement. These data also enable us to describe incoming replacement executives and compare them with the founders they replace. Among the fields captured in this data collection effort were the person’s years of work experience, whether the person had previously founded a startup, and education. Regarding education, we noted whether the person had a bachelor’s degree, master’s degree, MBA, MD, or PhD. Table 3 compares replaced founders with the new, incoming replacement managers along all of the fields we collected. The comparison suggests that replacement executives tend to have almost two years more experience than the replaced founders but are less than half as likely to have previously founded a startup. They are somewhat more likely to have an MBA and to have completed college. Replacements are more likely to have held CXO-level positions but have a CEO position. Table 3 Comparison of replaced founders and their replacements    Replaced founders  Replacements  Diff/s.e.  Years experience pre-startup  15.44  17.25  –1.803***           0.394  Number jobs on LinkedIn  4.481  5.520  –1.038***           0.126  Held CEO position  0.579  0.562  0.0176           0.0235  Past founder  0.601  0.165  0.436***           0.0206  Held CXO position  0.889  0.923  –0.0339**           0.0138  PhD  0.127  0.113  0.0143           0.0154  MD  0.0297  0.0123  0.0175**           0.00679  MBA  0.248  0.304  –0.0563***           0.0212  Master’s degree (including MBA)  0.435  0.448  –0.0127           0.0236  Bachelor’s degree  0.783  0.819  –0.0365*           0.0189  # LinkedIn connections (truncated)  297.7  307.6  –9.926           10.40  Number individuals  1,014  1,014  2,028     Replaced founders  Replacements  Diff/s.e.  Years experience pre-startup  15.44  17.25  –1.803***           0.394  Number jobs on LinkedIn  4.481  5.520  –1.038***           0.126  Held CEO position  0.579  0.562  0.0176           0.0235  Past founder  0.601  0.165  0.436***           0.0206  Held CXO position  0.889  0.923  –0.0339**           0.0138  PhD  0.127  0.113  0.0143           0.0154  MD  0.0297  0.0123  0.0175**           0.00679  MBA  0.248  0.304  –0.0563***           0.0212  Master’s degree (including MBA)  0.435  0.448  –0.0127           0.0236  Bachelor’s degree  0.783  0.819  –0.0365*           0.0189  # LinkedIn connections (truncated)  297.7  307.6  –9.926           10.40  Number individuals  1,014  1,014  2,028  We retrieved career histories for 1,322 of the 1,999 replaced founders, as well as their replacements, from LinkedIn (2,028 individuals in total). Table reports means, differences and two-sided t-statistic p-values for the replaced founders and the incoming replacement executives. All variables are measured at the time (year) of the startup’s founding. Table 1 defines the variables. Standard errors are reported in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. 1.2 Descriptives and correlates of founder replacement Before proceeding to our analysis of venture performance, we characterize founder replacement in our data. Table 4 shows the dynamics of founder replacement by financing round. As noted in the last row of Table 4, 15.1% of venture-backed firms in our sample experience a founder-replacement event (18.6% if we include those for which we cannot determine the date of the replacement). Founder replacement is less common in the first round, rises in the second round and continues well into the sixth round. Table 4 Founder replacement patterns    Round number     1  2  3  4  5  6+  Startups raising Nth round of funding  11,929  10,145  7,444  5,120  3,301  2,046  Startups achieving liquidity this round  860  941  785  598  404  499  Startups failing this round  1,510  1,257  839  531  321  421  Startups with founder replaced this round  429  599  400  229  121  131  Startups with founder replaced so far  429  1,008  1,379  1586  1,697  1,811  % startups with founder replaced this round  3.6%  5.9%  5.3%  4.5%  3.7%  6.4%  % startups with founder replaced so far  3.6%  8.4%  11.5%  13.2%  14.2%  15.1%     Round number     1  2  3  4  5  6+  Startups raising Nth round of funding  11,929  10,145  7,444  5,120  3,301  2,046  Startups achieving liquidity this round  860  941  785  598  404  499  Startups failing this round  1,510  1,257  839  531  321  421  Startups with founder replaced this round  429  599  400  229  121  131  Startups with founder replaced so far  429  1,008  1,379  1586  1,697  1,811  % startups with founder replaced this round  3.6%  5.9%  5.3%  4.5%  3.7%  6.4%  % startups with founder replaced so far  3.6%  8.4%  11.5%  13.2%  14.2%  15.1%  The table reports replacement rates across financing round sequence. Sample includes entrepreneurial firms tracked by VentureSource that satisfy the sample conditions in Section 1. The number of startups receiving an $$N$$th round of funding is lower than the number who received funding in a prior round, less exits, because some firms continue as private entities without raising subsequent financing. Next, we adopt a hazard specification of a particular founder being replaced as the data are right-censored and the phenomenon is observed on a continuous basis. Although we observe the exact date of a replacement, we create quarterly spells (results are robust to the use of monthly spells). We first account for characteristics of the founder, including whether that founder had a CXO title and whether there were any cofounders. We then track financing, including new rounds of funding, the overall level of funding to date, and whether the startup was profitable as of that round of financing. Recent financing rounds and the overall level of investment may proxy for the power of investors to replace founders. To further assess the role of investor power in replacing founders, we examine the number of directors who are investors. The board is explicitly tasked with hiring and firing the CEO and can exert significant influence over the hiring and firing of other executives. Similar studies of public firm boards, such as Weisbach 1988, show a direct connection between board size and investor power. Furthermore, the VC-backed entrepreneurial firm has a board of directors comprised of three different agents: independent observers, investors, and executives (see Kaplan and Strömberg 2003 for details). Analyzing board investor power requires the number of VCs who are directors in each round. VentureSource lists current/former board members, but dates of service are often missing. We identify an investor’s joining the board by their first investment in which either they are identified as the “lead”—or if they never have a lead position, their first investment in the firm. Identifying their exit from the board is more challenging as most will retain their position, although some early-stage VCs leave a board as the startup approaches an IPO. We date exits by the round where a known investor stops participating in financing events and a new investor takes a board seat.8 Finally, we create a dichotomous variable set to one if the board size is above the median outside board size (results are qualitatively similar with the continuous measure).9 Table 5 reports factors associated with the hazard of founder replacement. We find that the hazard of replacement is increasing not only in a new round of financing—whether in that quarter, as shown, or (in unreported results) during the previous two quarters —but also in the total amount of funding raised so far and in the number of investors on the board of directors. Consistent with Wasserman 2003, this suggests that investors indeed play a role in founder replacement, perhaps as a condition of a new round of funding or as part of their governance responsibilities as members of the board of directors. However, profitability is not associated with replacement in a statistically significant fashion. Founders holding a CXO role are more likely to be replaced than others. Table 5 Correlates of founder replacement    (1)  (2)  (3)  (4)  (5)  New financing round this quarter  0.265***  0.424***  0.316***  0.172**  0.264***     (0.0519)  (0.126)  (0.114)  (0.0678)  (0.0519)  Profitable at prior financing  0.0604  0.184  –0.404  0.116  0.0872     (0.109)  (0.182)  (0.342)  (0.156)  (0.109)  log capital stock at prior financing  0.153***  0.206***  0.104*  0.167***  0.151***     (0.0254)  (0.0587)  (0.0595)  (0.0337)  (0.0255)  Size of VC board  0.114***  0.169***  0.0567  0.115***  0.112***     (0.0192)  (0.0467)  (0.0459)  (0.0253)  (0.0194)  Founder held CXO role  0.264***  0.427***  0.355***  0.174***  0.266***     (0.0534)  (0.130)  (0.131)  (0.0669)  (0.0533)  Solo founder  0.0814  0.0449  –0.0477  0.202***  0.0985*     (0.0526)  (0.119)  (0.117)  (0.0706)  (0.0535)  Observations  411266  91715  79738  225869  411266  Log likelihood  –17067.4  –2542.6  –2570.7  –9643.8  –17061.3  Number of startups  11817  2941  2164  6334  11817  Industries  All  Consumer  Health care  IT  All  Industry FEs  N  N  N  N  Y     (1)  (2)  (3)  (4)  (5)  New financing round this quarter  0.265***  0.424***  0.316***  0.172**  0.264***     (0.0519)  (0.126)  (0.114)  (0.0678)  (0.0519)  Profitable at prior financing  0.0604  0.184  –0.404  0.116  0.0872     (0.109)  (0.182)  (0.342)  (0.156)  (0.109)  log capital stock at prior financing  0.153***  0.206***  0.104*  0.167***  0.151***     (0.0254)  (0.0587)  (0.0595)  (0.0337)  (0.0255)  Size of VC board  0.114***  0.169***  0.0567  0.115***  0.112***     (0.0192)  (0.0467)  (0.0459)  (0.0253)  (0.0194)  Founder held CXO role  0.264***  0.427***  0.355***  0.174***  0.266***     (0.0534)  (0.130)  (0.131)  (0.0669)  (0.0533)  Solo founder  0.0814  0.0449  –0.0477  0.202***  0.0985*     (0.0526)  (0.119)  (0.117)  (0.0706)  (0.0535)  Observations  411266  91715  79738  225869  411266  Log likelihood  –17067.4  –2542.6  –2570.7  –9643.8  –17061.3  Number of startups  11817  2941  2164  6334  11817  Industries  All  Consumer  Health care  IT  All  Industry FEs  N  N  N  N  Y  The table presents a hazard analysis of founder replacement. Observations are firm-founder-quarter triads, with failure defined as the founder being replaced in that quarter. Variables are as defined in Table 1. Columns 2–4 investigate individual industries. Standard errors are reported in parentheses and clustered at the startup level. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. We also see some differences among industries. Health care in particular differs from other industries in that neither the level of funding to date nor the size of the board predicts replacement. Also, solo founders are somewhat more likely to be replaced in IT startups, and more generally when industry fixed effects are included. 2. Does Founder Replacement Affect Performance? As noted above, Bernstein, Giroud, and Townsend (2016) establish a causal connection between investor activism and IPO/acquisition outcomes but do not demonstrate specific mechanisms as to how these benefits are achieved. Although prior work has shown that investors indeed replace founders of their portfolio companies (Kaplan, Sensoy, and Strömberg 2009; Hellmann and Puri 2002; Wasserman 2003), the only paper to draw a connection between founder replacement and venture outcomes is Chen and Thompson (2015), who stop short of claiming causality. To study the impact of founder replacement on firm outcomes, we measure the ultimate success of the firm. We extend the commonly used outcome variable—an IPO—to two more general measures of success. The first dependent variable is set to one for a portfolio that achieves an IPO or an attractive acquisition that exceeds 125% of total capital raised.10 An unattractive acquisition or failure of the firm both set the dependent variable to zero.11 Although 10% of firms achieve an IPO, some 20% of firms in our sample achieve a successful exit. The second outcome variable is the log of the observed exit valuation, which is set to 25% of capital raised if the startup failed. Exit valuation for nonfailures is either the final acquisition valuation or IPO market capitalization at the date of the offering.12 For firms without a reported exit valuation – predominantly acquired firms that were likely acquired for relatively low valuations – we treat the exit as a failure. This is not a strong assumption because the dummy variable above effectively does the same; moreover, Puri and Zarutskie (2012) show that many acquisitions are in fact hidden failures. These two dependent variables have a correlation of over 60%, however, the exit valuation provides an alternative continuous measure of success. The empirical model ties the founder replacement to outcome $$Y_{i}$$:   \begin{equation} \textrm{Y}_{i} = \rho_0 + \rho_1 R_{i} + \rho_2 X_{i} + \gamma_t + \phi_{\it State(i)} + v_{i}. \end{equation} (1) Here $$X_{i}$$ contains entrepreneurial firm characteristics such as firm age, syndicate size, profitability, and total capital raised. Time-varying measures are calculated either at each financing event, each quarter or at the last financing event prior to the time of the law changes we use in the instrumental variable analysis. It will also capture fixed effects for founding year, stage (round number) and industry. State fixed effects are captured with $$\phi_{\it State(i)}$$ and $$\gamma_t$$ represents financing year fixed effects. The variable $$R_{i}$$ indicates whether a founder was replaced. The unit of observation is an entrepreneurial firm. Table 6 estimates this equation on the full sample of startups as described above.13 As is visible from Column 1, there is a strong negative correlation between founder replacement and favorable outcomes. Column 2 repeats the exercise for CXO replacements only. Columns 3 and 4 consider the log exit valuation defined above and thus measures the size of a liquidity event. The results are similar to those in the first two columns, suggesting again that startups where a founder was replaced tend to underperform on average. Table 6 Full sample exit outcomes and founder replacement    IPO/Acq.?  log exit value     (1)  (2)  (3)  (4)  Founder replaced?  –0.0472**     –0.211**        (0.0198)     (0.0881)     Founder-CXO replaced?     –0.0577***     –0.289***        (0.0170)     (0.0773)  Constant  0.302***  0.300***  –0.475  –0.486     (0.0551)  (0.0553)  (0.407)  (0.408)  Observations  11401  11401  11184  11184  $$R^{2}$$  0.0616  0.0619  0.352  0.352  State FEs  Y  Y  Y  Y  Founding year FEs  Y  Y  Y  Y  Industry FEs  Y  Y  Y  Y  Industry $$\times$$ Founding Year FEs  Y  Y  Y  Y  Team size FEs  Y  Y  Y  Y     IPO/Acq.?  log exit value     (1)  (2)  (3)  (4)  Founder replaced?  –0.0472**     –0.211**        (0.0198)     (0.0881)     Founder-CXO replaced?     –0.0577***     –0.289***        (0.0170)     (0.0773)  Constant  0.302***  0.300***  –0.475  –0.486     (0.0551)  (0.0553)  (0.407)  (0.408)  Observations  11401  11401  11184  11184  $$R^{2}$$  0.0616  0.0619  0.352  0.352  State FEs  Y  Y  Y  Y  Founding year FEs  Y  Y  Y  Y  Industry FEs  Y  Y  Y  Y  Industry $$\times$$ Founding Year FEs  Y  Y  Y  Y  Team size FEs  Y  Y  Y  Y  The table reports ordinary least-squares (OLS) regressions of firm-level outcomes on indicators for whether the startup had one of two types of founder replacement. The unit of observation is a VC-backed startup. “Founder replaced?” is equal to one if at least one of the founding team members was observed replaced before the exit or end of the sample. “Founder-CXO replaced?” is one if one of those replaced had the CXO title (e.g., Chief Technology Officer [CTO], CFO, or CEO). The dependent variable in Columns (1) and (2) is a dummy equal to one if the firm had an IPO or acquisition with a valuation greater than 1.25 times the capital invested by the end of the sample period (April 2017). The last two columns report the log of exit valuation (if known, otherwise assumed to be 25% of invested capital). If unknown, exit value is assumed to be 25% of capital invested. Fixed effects include the headquarters state, founding year, industry, the interaction of industry and founding year and indicators for the size of the founding team. Unreported is a control for the log of first capital invested. Standard errors clustered at the founding year reported in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. We cannot draw causal conclusions from Table 6 for several reasons. Venture capitalists may be more likely to replace founders when their startups are struggling, and founders may be more likely to relinquish their roles when prospects appear bleak. We propose an instrumental variables approach below. 3. Instrumental Variables The replacement variable $$R_{i}$$ is likely correlated with the current and future prospects of the entrepreneurial firm, both omitted from (1). For example, replacement may coincide with unobserved negative shocks to the firm that would lower future performance or VC investors may seek to replace founders only in firms that have better prospects unconditionally. We require a variable $$Z$$ that predicts the likelihood of replacement but does not belong in Equation (1) (i.e., exclusion restriction). Our instrument proxies for changes to the supply of potential replacement executives from other companies using plausibly exogenous changes to the ease of their recruitment. As finding replacement executives is nontrivial, changes to the pool of available executives could affect the both rate of founder replacement and the quality of replacements recruited. Some of the most attractive replacement executives will be those with experience at the sort of company that might acquire the focal startup, especially for a private firm that may be struggling and for whom an acquisition might seem the most promising exit. Table A1 in the Online Appendix shows the most frequent prior employers of the incoming replacement executives in our sample are large, established firms. This is consistent with the “professionalization” notion that new, incoming replacements are not fresh entrepreneurial blood but rather seasoned executives from established firms. Given that these large firms are an attractive source of replacement executives, exogenous changes to inter-organizational mobility act as a shock to the supply of replacement executives for VC-backed firms.14 In an ideal experiment, the researcher would randomly restrict the ability for the firm or VC to replace a founder of their choice. For example, one could simply impose a no-firing rule or otherwise restrict labor mobility in the firm’s industry. Doing so eliminates any selection issues (e.g., the VC picks the companies that have the best prospects to replace, or those that need replacement are worse firms) and can isolate causal effects. Our proposed instrument exploits changes in labor laws that, in turn, may affect the supply of replacement executives. There are three possible outcomes. First, the cause of the firm’s struggles could be the “jockey” (i.e., current management) and not the “horse” as suggested by Kaplan, Sensoy, and Strömberg (2009) in their analysis of firms that eventually have an IPO. The VC may not have already replaced management, either because they want to be perceived as patient or because the management team is entrenched. Second, replacement might improve firm prospects because the existing match between the founder and the firm limits growth and exit opportunities. Third, replacement could have a negative impact on performance if founders are important assets and the VC incorrectly assesses their value. 3.1 Employee non-compete agreements and executive replacements One factor affecting the inter-organizational mobility of replacement executives is policy regarding post-employment covenants not to compete. Non-compete agreements are sections of employment contracts in which a worker covenants neither to join nor to found a rival firm within 1–2 years of leaving. A growing body of work shows that non-compete agreements bind employees to their employers, thus making it difficult for small companies to attract workers away from established firms (Stuart and Sorenson 2003). Garmaise (2011) shows that firms use non-compete agreements with at least 70% of their top executives, who are likely candidates to be targeted as replacements for founders (e.g., Table A1 in the Online Appendix). Marx, Strumsky, and Fleming (2009) provide causal evidence linking the enforceability of non-compete agreements to worker mobility, leveraging an unintentional 1985 reversal of non-compete policy in Michigan. These shocks to the supply of executives should—given fixed demand—alter the VC’s opportunity cost of either replacing or retaining the existing founding team. Importantly, non-compete agreements are more likely to be enforced against top or high-quality management that the established firm most wants to retain. Thus, the changes induced by the law will increase or decrease the supply of higher-quality replacement executives. The Michigan reversal occurred well in advance of our sampling period, but several changes in other states facilitate analysis using our data. Our methodology for finding changes in non-compete policy is as follows. We reviewed Malsberger, Brock, and Pedowitz (2016), the definitive reference regarding both legislative and judicial changes to state-by-state policy regarding non-compete agreements, and made a list of changes during the time period of our data set. We also searched Lexis/Nexis for state Supreme Court decisions possibly affecting non-compete agreements. Approximately three dozen legislative or judicial changes appeared potentially material. We then enlisted the expertise of two prominent employment lawyers to assess the impact of these, leaving 14 material shifts to enforceability during our time period. During our sample period, nine states strengthened the enforceability of employee non-compete agreements: Florida (1996), Ohio (2004), Vermont (2005), Idaho (2008), Wisconsin (2009), Georgia (2010), Colorado (2011), Illinois (2011), and Texas (2011). Importantly, we require that the law changes were not related to the future prospects of the startups in the state. For changes due to decisions not handed down by a state Supreme Court, which are plausibly exogenous, we provide background on the political economy of the change. Florida (1996): The change in Florida was pushed for (and codrafted by) the Florida Bar Association, as attorneys in the state had become frustrated with the lack of clarity regarding enforceability of employee non-compete agreements and found it difficult to advise their clients with certainty, and not for the purpose of affecting startup outcomes.15 Ohio (2004): In Lake Land v. Columber, the state Supreme Court resolved a dispute between various courts of appeals in the state regarding whether continued employment was sufficient consideration to uphold a non-compete. Following this decision, firms no longer had to offer particular consideration (e.g., compensation, training, or promotion) when asking an existing employee to sign a non-compete. Vermont (2005): Similar to Ohio’s 2004 verdict, the decision in Summits 7 v. Kelly resolved a division among local trial courts by stating that continuing employment is sufficient consideration for a so-called “afterthought” non-compete requested after an employee starts working. Idaho (2008): The Idaho law, which among other provisions enacted what is commonly called a “blue-pencil” rule whereby which a judge facing a lawsuit is allowed to modify the contract to make it more reasonable, was advocated by the Idaho Falls based Melaleuca health products company (Hopkins 2008). Wisconsin (2009): The State Supreme Court decision in Star Direct v. Dal Pra had a significant impact on enforceability by upholding “red pencil” reformation of contracts. Without reformation, judges would refuse to enforce unreasonable non-compete agreements. With red-pencil reformation, a judge can strike unacceptable parts of the contract but retain the rest. Such a capability may give firms incentives to write unreasonable contracts that yield an in terrorem “chilling effect” among employees but are nonetheless partially enforced in court. A 2015 decision further strengthened enforceability by confirming that continued at-will employment sufficed as consideration for a post-hire non-compete. Georgia (2010): Georgia added a blue-pencil provision, with its change brought about by a 2010 referendum which amended the state constitution.16 However, the text of the referendum has been criticized as misleading as it did not make direct reference to employee non-compete covenants, so the reversal can reasonably be characterized as unanticipated.17 Colorado (2011): The state Supreme Court ruling in Luncht’s Concrete Pumping v. Horner brought Colorado into the predominant practice that continued employment is sufficient consideration for a non-compete, as opposed to requiring additional compensation (or a promotion) in exchange for signing the non-compete after having already started at the firm. Illinois (2011): The state Supreme Court decision in Reliable Fire Equipment v. Arredondo fundamentally changed how enforceable non-compete agreements are in Illinois. Previously, the state had imposed stringent requirements for establishing a “legitimate business interest”, but Reliable Fire changed the old rigid test into a more flexible one, making it easier to enforce non-compete agreements. Texas (2011): The state Supreme Court decision in Marsh v. Cook aligned Texas non-compete law with other states with respect to consideration. Prior the decision, the consideration had to “give rise” to the interest being protected, which resulted in very little actually be protectable (primarily just trade secrets). Marsh changed that test: thereafter, consideration for a non-compete could be far more broad. Thus Texas became a state where it is not nearly as hard as it had been to have an enforceable non-compete. During the same period, five states weakened the enforceability of non-compete agreements: Louisiana (2001), Oregon (2008), South Carolina (2010), New Hampshire (2012), and Kentucky (2014).18 Louisiana (2001): The changes in Louisiana was enacted by the Supreme Court, which in Shreveport Bossier, Inc. v. Bond ruled that the state’s non-compete agreements could only restrict entrepreneurship and not simply moving to a rival firm. That the change was enacted by the SSC cannot be reasonably construed as anticipating future startup performance. (Note that this change was partially undone in 2003 by a new law.) Oregon (2008): Oregon’s Commissioner of Labor successfully lobbied to passed a bill that would invalidate non-compete agreements if workers were not told about the covenant until after they accepted their offer out of employment.19 South Carolina (2010): In Poynter Investments v. Century Builders of Piedmont, the state Supreme Court ruled against the use of “blue pencil” provisions whereby a court can reform (i.e., soften the terms of) an unenforceable non-compete instead of striking it down as invalid. At the same time, the Court made it easier for firms to obtain a preliminary injunction against ex-employees, so the impact of the SC ruling may be tempered. (Results are robust to treating SC as weakening enforceability, strengthening it, or not affecting it.) New Hampshire (2012): A similar measure was brought about in 2012 by a New Hampshire state representative who had personally been negatively affected by a non-compete,20 suggesting that this reform was undertaken not out of a desire to promote the performance of startups but rather as a workers’ rights measure. Kentucky (2014): In Creech v. Brown the state Supreme court ruled that continued employment was not sufficient consideration for a non-compete entered into after an employee started work at a new firm. In sum, the changes in non-compete enforceability appear not to have been motivated by the prospects of startups in those states. By contrast, Hawaii’s 2015 reform, which banned non-compete agreements in the IT industry, was explicitly taken up in order to foster entrepreneurial activity. Our instrumental variable captures these labor law changes across time and US states in our sample period. Defined in detail below, the variable identifies whether a startup active in a given state experienced a change in non-compete law—whether strengthening or weakening—or had no change in labor laws. For the set of startups in states that weakened non-compete laws, we expect such a change to make it relatively easier to replace founders. Alternatively, those states that strengthened their non-compete rules should exhibit relatively fewer replacements as the supply of possible replacement executives is smaller. 3.2 External validity Are these states in which non-compete laws changed representative of VC-backed firms during our sample period? The 14 states with non-compete reforms used in our analysis comprise 17.2% of overall VC investments. Given that 41.4% of all VC investments are in California, the treated states compose nearly 30% of the remaining startups in the United States. Moreover, 32.1% or nearly one-third of all venture capitalists have portfolio companies in the treated states. Table 7 compares more variables for startups in the treated states to those in all other states in our sample period. The third column reports the full sample means for each variable. The first observable differences show up in capital raised. Startups in treated states raise nearly a million dollars more in their initial round but $5MM less during their lifetime, although startups in both types of states have a similar number of rounds. Startups in treated states have lower rates of IPOs and acquisitions though similar failure rates as untreated states. This difference means that the treated firms in the IV regression start with a lower chance of success as measured by the dependent variable. Rates of founder replacement are roughly equivalent between treated and untreated states. Table 7 Comparison of VC activity in IV versus non-IV states    Never treated  Treated state  Total  Year firm founded  2001.1  2000.7  2001.0  Year first VC  2002.5  2002.5  2002.5  First capital raised  6.303  7.285  6.472  Total equity financings (all)  3.538  3.478  3.528  Total capital raised (m)  38.42  33.43  37.56  Information technology  0.539  0.523  0.536  Biotech  0.185  0.174  0.183  Went public  0.0637  0.0438  0.0603  Acquired  0.414  0.409  0.413  Still private  0.242  0.245  0.242  Out of business  0.280  0.301  0.284  Founder replaced?  0.153  0.146  0.152  Portfolio size of VC investor  82.91  63.57  79.58  Firm raised from top 10% VC  0.699  0.590  0.680     Never treated  Treated state  Total  Year firm founded  2001.1  2000.7  2001.0  Year first VC  2002.5  2002.5  2002.5  First capital raised  6.303  7.285  6.472  Total equity financings (all)  3.538  3.478  3.528  Total capital raised (m)  38.42  33.43  37.56  Information technology  0.539  0.523  0.536  Biotech  0.185  0.174  0.183  Went public  0.0637  0.0438  0.0603  Acquired  0.414  0.409  0.413  Still private  0.242  0.245  0.242  Out of business  0.280  0.301  0.284  Founder replaced?  0.153  0.146  0.152  Portfolio size of VC investor  82.91  63.57  79.58  Firm raised from top 10% VC  0.699  0.590  0.680  The table reports startup and investor observables for two samples. The first column (“Never treated”) reports means of each variable for the states that did not have a non-compete law change in our sample period. The second column (“Treated state”) reports the same means for the states with such law changes. The last column (“Total”) reports the full sample means. “Portfolio size of VC investor” is the count of number of unique entrepreneurial firm investments made by the startup’s investors as of the firm’s exit. The variable serves as a proxy for experience. The variable “Firm raised from top 10% VC” is one if at least one of the entrepreneurial firm’s investors was in the top 10% of this portfolio size variable. Table 1 defines the other variables. A key feature of the data construction for the IV analysis described below is the use of portfolio firms belonging to VCs who invested in startups treated by the changes in non-compete law. The variable “Portfolio size of VC investor” shows that VCs investing in treated states have 19% smaller portfolios. The variable “Firm raised from top 10% VC” is one if at least one of a startup’s investors is in the top 10% of investing experience by the end of the sample. Treated-state startups are nearly 11% less likely to have such an investor. This difference is as expected, but we believe reasonably close. Overall, there do not appear to be large economic differences in observables between firms and investors in the treated states. Thus we believe the IV results generalize to the average VC-backed firm in our sample period. 3.3 Is there home bias in hiring? We take as our treatment group startup companies active and VC-backed in these 14 states at the time these legal changes took effect. For the non-compete reversals above to have affected the ability of startup companies in those states to recruit replacement executives, there must be a material “home bias” in recruitment. In other words, although startups could (and do) recruit replacement executives from other states, the non-compete reversal should have an effect only if the startups disproportionately recruit replacement executives from the same state where they are located. To establish home bias, it is not sufficient to merely count the proportion of replacement executives that come from the same state, as states have different supplies of potential replacements. We proceeded to build a baseline of the percentage of public firms in each state in order to inform the likelihood that a replacement executive would come from the same state as the focal startup. We did this for the IT and Health care sectors, for which we could match directly the classification codes from VentureSource to Compustat. IT and Health care represent 68% of all VC-backed ventures in our full sample. The next step was to compare the same-state replacement rate for IT and Health care startups in each state to the percentage of public companies in those states to determine whether there is a “home bias.” This required looking up the location of the replacement executives. A research assistant was tasked with finding the prior work location—not simply the company headquarters—of all 1,991 replacement executives. Sources included LinkedIn, ZoomInfo, BusinessWeek, and others. Reliable data was available for 1,373 replacement executives; the remainder were either not locatable or could not be disambiguated between multiple locations. For the replacement executives for whom we could not reliably establish their previous geographical location, the firms that hired them did not differ significantly in terms of year of founding, the amount of capital raised in the first round, or the total rounds of funding. We find substantial “home bias” in the recruitment of replacement executives. First of all, every state with at least ten replacements (and all but one state with five or more replacements) has evidence of a home bias. Even in California, which as mentioned above is home to 26% of public IT and Health care companies, there is a home bias of more than double as 65% of replacement executives are recruited from within the state. Moreover, we note that each of the states with a non-compete reversal used for our instrument exhibits a home bias from 8.6 to 15 times.21 Of course, the above does not control for possibly confounding factors, so we next turn to multivariate analysis. Table 8 analyzes several sources of bias in the selection of replacement executives. For each replacement, we have 50 observations corresponding to U.S. states. The dependent variable is set to one if the replacement for that focal firm’s departing founder came from that state. Column (1) formally tests our home bias hypothesis. The estimate of the coefficient on the startup being in the focal state is positive and statistically significant in all models. The marginal effect on the probability of the replacement coming from that same state is 7.9%. In Column (2), we add additional VC-related controls, including whether the VC is in the same state as the replacement and the (logged) count of the VCs investments in that state. Although both of these are estimated with positive and statistically significant coefficients, their marginal effects are an order of magnitude smaller than home bias. Table 8 Geographic bias in recruitment of replacements for founders    Replacement executive from state?     (1)  (2)  (3)  (4)  Startup in focal state?  2.436***  1.689***  1.630***  1.578***     (0.0439)  (0.0547)  (0.0624)  (0.0640)  Any of startup’s VCs in focal state?     0.572***  0.365***  0.288***        (0.0419)  (0.0502)  (0.0511)  Log first capital raised     0.0616***  0.0303**  0.0220*        (0.0126)  (0.0122)  (0.0118)  Total financings     –0.0151***  –0.00697*  –0.00340        (0.00428)  (0.00419)  (0.00400)  log total capital raised     –0.0722***  –0.0627***  –0.0520***        (0.0124)  (0.0118)  (0.0111)  log # investments of startup’s     0.147***  0.0545***  0.0190***  $$\quad$$ VCs in focal state     (0.00648)  (0.00625)  (0.00593)  log # public firms in industry        0.271***  –0.514***  $$\quad$$ in focal state        (0.0184)  (0.122)  Constant  –2.357***  –2.707***  –3.844***  –4.010***     (0.0533)  (0.0929)  (0.127)  (0.404)  Observations  74850  73300  57850  43966  Pseudo-$$R^{2}$$  0.338  0.405  0.442  0.432  Number startups  1373  1345  1054  1054  Industries  All  All  IT, Health care  IT, Health care  Founding year FEs  Y  Y  Y  Y  Year 1st fin. FEs  Y  Y  Y  Y  Industry FEs  Y  Y  Y  Y  Replacement state FEs  N  N  N  Y     Replacement executive from state?     (1)  (2)  (3)  (4)  Startup in focal state?  2.436***  1.689***  1.630***  1.578***     (0.0439)  (0.0547)  (0.0624)  (0.0640)  Any of startup’s VCs in focal state?     0.572***  0.365***  0.288***        (0.0419)  (0.0502)  (0.0511)  Log first capital raised     0.0616***  0.0303**  0.0220*        (0.0126)  (0.0122)  (0.0118)  Total financings     –0.0151***  –0.00697*  –0.00340        (0.00428)  (0.00419)  (0.00400)  log total capital raised     –0.0722***  –0.0627***  –0.0520***        (0.0124)  (0.0118)  (0.0111)  log # investments of startup’s     0.147***  0.0545***  0.0190***  $$\quad$$ VCs in focal state     (0.00648)  (0.00625)  (0.00593)  log # public firms in industry        0.271***  –0.514***  $$\quad$$ in focal state        (0.0184)  (0.122)  Constant  –2.357***  –2.707***  –3.844***  –4.010***     (0.0533)  (0.0929)  (0.127)  (0.404)  Observations  74850  73300  57850  43966  Pseudo-$$R^{2}$$  0.338  0.405  0.442  0.432  Number startups  1373  1345  1054  1054  Industries  All  All  IT, Health care  IT, Health care  Founding year FEs  Y  Y  Y  Y  Year 1st fin. FEs  Y  Y  Y  Y  Industry FEs  Y  Y  Y  Y  Replacement state FEs  N  N  N  Y  The table analyzes possible sources of geographic bias in the recruitment of replacements for 1,999 founders. Each observation is a replacement-state dyad, 50 observations per founder replacement. The dependent variable is 1 if the incoming replacement for the founder at a given startup was recruited from that state. “Startup in focal state?” captures whether the startup is headquartered in the focal state (i.e., the state for that replacement-state dyad). “Any of startup’s VCs in focal state?” captures whether some VC that invested in the focal startup is headquartered in the focal state. “Log # investments of startup’s VCs in focal state” reports the number of investments in the focal state made by all of the VCs who invested in the focal startup. Columns (1) and (2) are estimated on the full sample of founder replacements. The sample in Columns (3) and (4) is estimated on founder replacements at IT and Health care startups because direct matches to Compustat counts of public firms are available only for those two categories. “Log # public firms in industry in focal state” is the number of firms in either IT or Health care that were in the focal state (for IT or Health care startups, respectively). Table 1 defines the other variables. Robust standard errors are reported in parentheses, clustered at the state level. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. Column (3) introduces a control for the number of public firms in the same state as the replacement. Doing so requires mapping industry categories from VentureSource to Compustat. The only two categories that map directly are Information Technology and Health care, so the remainder of the table is restricted to these industries. Like in the previous column, although there is a positive association between the likelihood of replacement and the presence of public firms from the same industry (at least for IT and Health care), the estimated coefficient is again an order of magnitude smaller than for home bias. Column (4) adds state fixed effects, with consistent results. 3.4 IV sample construction Within the treated states, we consider two sets of startups. First, we construct a sample of startups affected by the change in labor laws. Startups must receive their first round of capital before the law change, still be active (nonexited) by this date and have had no founder replacements. These startups are at risk of replacement and are affected by the change in the labor supply from the enforceability change. Note that we do not select firms based on any post-law-change behavior (including follow-on investments) as such could introduce confounds from selection into treatment. Similarly, including startups founded or first financed after the law change introduces both selection (i.e., different firms are founded because of the new law) and the treatment effects of interest. The next challenge in satisfying the exclusion restriction is the comparison or control sample. We cannot simply track the same entrepreneurial firm over time because once a founder is replaced in a single-founder firm (a large fraction of the sample), the firm can no longer receive treatment. Rather, we require some set of firms that were not affected by the law yet were at risk of having their founders replaced. Such firms would ideally face similar economic and legal settings as those startups affected by the law change. That is, we would like to compare these treated startups to ones based in the same state, financed at the same time and in the same industry but for some random reason are not affected by the labor law change. Such a sample is not available, but we present an alternative that exploits both within and across-state variation. One approach would be to include all startups not affected by the law changes, but doing so would likely introduce a large set of unobservably dissimilar firms, particularly with regard to unobserved trends. Such trends might capture changes in startup success instead of the proposed treatment effect. Our approach exploits knowledge about the treated startups’ investors and their portfolios. Constructing the control group proceeds by identifying all VC investors of the treated startups defined above. Rather than include all VC-backed firms financed during the same years, we narrow the sample to those in the portfolios of these VC investors who invested in treated startups and who were headquartered in one of the treated states. Such a restriction excludes VCs who for example only invested in California or only in Washington (both states had no law change). How does the restriction of VC portfolios with some treatment exposure help address identification issues? The tendency of VCs to invest in similar-quality startups within an industry helps to ensure that the treated and control startups exhibit similar unobserved trends. VCs in our sample also typically invest out of a fund or two, of which each selects startups of similar development stage and industry. Controlling for firm founding year, firm state headquarters, financing stage, total capital raised and round number addresses cross-sectional differences in firm maturity that could affect replacement rates. Estimation of Equation (3) using this sample mimics estimators that exploit staggered law changes. The main difference here is that we do not include startups financed after the law changes because the law change likely affected both the types of startups financed and their ability to replace managers. We thus need to focus on a sample of startups who were founded and financed before the law changes but that have differential exposure to the changes. Startups in treated states act as controls for within-state startups and other startups financed at the same time. The inclusion of state fixed effects allows us to control for time-invariant differences across the treated states, while implying that identification of the effect of replacement comes from within-state variation before the law change year. Inclusion of startups outside of treated states in a model that also includes state fixed effects would not provide any identification for the instrumental variable and are thus excluded. Table 9, Column (1) presents the results of the Equation (1) estimated using the sample of startups in treated states. This table shows a negative and statistically significant association between replacing founders and eventually achieving an attractive liquidity event, consistent with Table 6 above. Thus it does not appear that the IV sample is materially different from the overall sample in this respect. As discussed above, this correlation could be downward biased given that investors are more likely to dismiss founders in struggling companies (or that founders are also more likely to resign voluntarily, necessitating their replacement). Table 9 Founder replacement and firm outcomes: Instrumental variables    IPO/Acq.?  Replaced?  IPO/Acq.?  log exit value     OLS  First stage  2SLS  OLS  2SLS     (1)  (2)  (3)  (4)  (5)  Founder replaced  –0.0451*     0.232**  –0.202  1.399**     (0.0236)     (0.112)  (0.132)  (0.592)  Increased Enforceability     –0.758***                 (0.127)           Log capital stock  0.0307**  0.306***  0.0146*  1.129***  1.037***     (0.0111)  (0.0373)  (0.00839)  (0.0354)  (0.0496)  Syndicate size  0.00148  0.0529  –0.00361  0.0530  0.0272     (0.0129)  (0.0860)  (0.0173)  (0.0787)  (0.0821)  Profitable at financing  –0.00154  –0.190*  0.0130  0.0508  0.133     (0.0212)  (0.104)  (0.0235)  (0.100)  (0.108)  Constant  0.203**  –1.779***  –0.121*  –1.320*  –2.700***     (0.0853)  (0.499)  (0.0725)  (0.709)  (0.449)  Observations  1341  1341  1341  1326  1326  $$R^2$$  0.0472  0.191  .  0.516  .  1st stage F-stat     35.42           Financing year FEs?  Y  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Y  Round # FEs?  Y  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  Y     IPO/Acq.?  Replaced?  IPO/Acq.?  log exit value     OLS  First stage  2SLS  OLS  2SLS     (1)  (2)  (3)  (4)  (5)  Founder replaced  –0.0451*     0.232**  –0.202  1.399**     (0.0236)     (0.112)  (0.132)  (0.592)  Increased Enforceability     –0.758***                 (0.127)           Log capital stock  0.0307**  0.306***  0.0146*  1.129***  1.037***     (0.0111)  (0.0373)  (0.00839)  (0.0354)  (0.0496)  Syndicate size  0.00148  0.0529  –0.00361  0.0530  0.0272     (0.0129)  (0.0860)  (0.0173)  (0.0787)  (0.0821)  Profitable at financing  –0.00154  –0.190*  0.0130  0.0508  0.133     (0.0212)  (0.104)  (0.0235)  (0.100)  (0.108)  Constant  0.203**  –1.779***  –0.121*  –1.320*  –2.700***     (0.0853)  (0.499)  (0.0725)  (0.709)  (0.449)  Observations  1341  1341  1341  1326  1326  $$R^2$$  0.0472  0.191  .  0.516  .  1st stage F-stat     35.42           Financing year FEs?  Y  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Y  Round # FEs?  Y  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  Y  The table reports OLS and 2SLS estimates for founder replacement and startup outcomes in the 14 states that experienced changes in the enforceability of employee non-compete agreements. The unit of observation is a startup headquartered in one of these states and first financed before the non-compete changes. The sample of startups is described in Section 3. Column (1) regresses a dummy variable for whether a startup has an IPO or attractive acquisition on a set of controls. The control “Founder replaced” is one if a startup had at least one founder replaced on the executive team. “Increased Enforceability” corresponds to whether the state in which a focal startup is headquartered changed its non-compete laws; values of 1, and $$-1$$ represent an increase in enforceability and a decrease in enforceability, respectively. Other controls are as defined in Tables 1. Column (2) reports the first stage probit estimates where the replacement dummy is instrumented by “Increased Enforceability” given the policy change in that startup’s state. “1st. stage F” is the Cragg-Donald Wald F weak instruments statistic. Column (3) reports the two-stage least squares second-stage estimates. Columns (4) and (5) have instead as the dependent variable the log of the exit valuation (set to 25% of capital raised if the firm failed, had an unknown exit valuation or was still private by the end of the sample). “Financing year FEs” are fixed effects for the financing year prior to the reference law change year and “Round # FEs” are fixed effects for the financing round number. “Industry FEs” are fixed effects for the seven major industries in VentureSource. “Founding year FEs” are fixed effects for the startup’s founding year. “State FEs” are fixed effects for the startup’s headquarter state. Robust standard errors are reported in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. 3.5 Empirical model If changes in the enforceability of non-compete agreements affect the supply of available executives, then they should predict differential founder replacement after the law change for treated firms compared to control firms. Let the variable $$I_{i}$$ represent if and how non-compete enforceability changed for a startup active in a treated state, taking on values ${$-$ 1, 0, 1}$ which correspond to loosening of enforceability, no change, and tightening enforceability (similar to the variable in Garmaise 2011). Startups that either exited or had a founder replacement before their state’s non-compete change will have $$I_{i}$$ set to zero. Thus, this variable can be separately identified from the state fixed effects. The reduced form first stage regression that relates replacement to changes in non-compete laws is then:   \begin{equation} \text{R}_{i} = \rho_0 + \rho_1 X_{i} + \rho_2 I_{i} + \gamma_t +\phi_{\it State(i)} + \epsilon_{i}. \end{equation} (2) Again, $$R_{i}$$ is whether a founder was replaced after the focal policy reversal. $$X_{i}$$ are firm $$i$$ controls such as capital raised, syndicate size, and profitability. The $$X_i$$ also include round and industry fixed effects, while $$\gamma_t$$ is the financing year fixed effect and $$\phi_{\it State(i)}$$ is the state fixed effect. The estimate of $$\rho_2$$ reveals whether there is a reduced form correlation between changes in non-compete enforceability and founder replacement ($$R_{i}$$). We predict that increased enforceability should lead to relatively fewer replacements ($$\rho_2 < 0$$). The second stage is now:   \begin{equation} \textrm{Y}_{i} = \delta_0 + \delta_1 R_{i} + \delta_2 X_{i} + \gamma_t + \phi_{\it State(i)} + u_{i}. \end{equation} (3) where $$R_i$$ is instrumented from Equation (2). The dependent variable $$Y_i$$ includes the exit outcomes studied in Table 6: whether the startup achieves a quality exit, and also the log exit value. Table 9 contains the results of our instrumental variable regression, first for the liquidity outcome and then for the log value of the exit. Column (2) presents the first stage estimates of (2) used in the two stage least squares.22 The estimate of the coefficient on “Increased Enforceability” (i.e., $$\rho_2$$) is economically and statistically significant, with the predicted negative sign. The weak instruments F-statistic (e.g., Stock and Yogo 2005) exceeds the conventional required level. The results suggest that founder replacement is indeed sensitive to the supply of available executives in the same state who might take the founder’s executive role. The sign on the IV is also as expected: increased enforceability correlates with a lower probability of replacement. The second-stage estimate in Column (3) presents the instrumented coefficient for replacements $$R_{i}$$.23 Two results emerge. First, the coefficient is positive and significant, suggesting a positive treatment effect. Second, the sign of the coefficient on founder replacement reverses between the naive regression in Column (1) and also in Table 6, where it is negative, and the 2SLS result in Column (3), where it is positive. The economic magnitude of the estimate can be determined by the predicted probability of replacement from the first stage in column (2). A one-standard-deviation shift in this probability of predicted replacement (14%) implies a 25% increase in the probability of a liquidity event relative to the mean. The reversal of coefficient signs between the naive OLS and 2SLS imply a downward bias, which likely stems from a selection of relatively worse firms requiring VC intervention through founder replacement.24 The estimates suggest a positive causal effect of founder executive replacement in VC-backed firms. In the remaining columns of Table 9 we examine an alternative dependent variable: log of the exit value. Here, the naive cross-sectional analysis in Column (4) would indicate that founder replacement correlates with worse exit valuations. These patterns reassuringly resemble those of Table 6. Again, the second-stage estimates in Column (5)—the first stage is identical to Column (2)—show a positive correlation between replacement and exit values. 4. Decomposing the Positive Impact of Replacement on Venture Outcomes The results in Table 9 demonstrate a positive causal effect of founder replacement of firm exit outcomes. In this section, we attempt to disentangle how this value is created. Although we saw above a correlation between investor power and replacement (Table 5), we cannot state categorically that all replacements are involuntary. Rather, it may be that some founders relinquish their roles voluntarily but stay on, contributing in a different capacity. The combined human capital of an original founder and “new blood” may represent a net positive for the firm, suggesting that the benefit is more of an augmentation story about bringing in new executives to increase the pool of skills, and with founders making accommodations for those new executives by taking on a new formal role (even if their day-to-day responsibilities change little). Such a story would stand in contrast to the “professionalization” story of Hellmann and Puri (2002). Alternative explanations might also include that the incoming executives act in large part as “coaches” for the original founders, grooming them on a temporary basis so that they can later re-assume their former responsibilities. To assess the mechanisms at play, we decompose our instrumental-variables analysis along two axes: the replaced founder’s role and whether the replaced founder stays with the firm. We first exploit variation in the types of founders replaced, by using their titles prior to replacement. As is visible in Table 5, those who hold a CXO role are considerably more likely to be replaced than others. It is plausible that replacing top executives who have more decision-making power at the firm should have bigger benefits to the firm than replacing lower-level executives. Columns (1) and (2) of Table 10 consider two alternative indicators for replacement that split the main variable from Table 9: founders with CXO titles and those with titles below this rank (i.e., VP level).25, The positive causal effect of replacement is stronger in Column (1). Note that we cannot reject the null that coefficients across Columns (1) and (2) are different due to the naturally large standard errors in IV. In fact, they capture different types of replacement. Table 10 Differences in the effects of replacement    Founder type  Separating versus Accommodating     (1)  (2)  (3)  (4)  Founder-CXO replaced  0.326**              (0.163)           Non-CXO founder replaced     0.543              (0.488)        Founder replaced and left        0.290*              (0.164)     Founder replaced and stayed           0.714              (0.533)  Constant  –0.115  –0.101  –0.113  –0.0886     (0.101)  (0.0760)  (0.102)  (0.0784)  Observations  1287  1120  1210  1120  Controls?  Y  Y  Y  Y  Financing years FE?  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Round # FE?  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y     Founder type  Separating versus Accommodating     (1)  (2)  (3)  (4)  Founder-CXO replaced  0.326**              (0.163)           Non-CXO founder replaced     0.543              (0.488)        Founder replaced and left        0.290*              (0.164)     Founder replaced and stayed           0.714              (0.533)  Constant  –0.115  –0.101  –0.113  –0.0886     (0.101)  (0.0760)  (0.102)  (0.0784)  Observations  1287  1120  1210  1120  Controls?  Y  Y  Y  Y  Financing years FE?  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Round # FE?  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  The table reports additional specifications of the instrumental variables model in Table 9. The main replacement variable “Founder-CXO replaced” variable in Column (1) is a dummy if a replacement occurs and the replaced founder had a title of CXO (e.g., CFO or CEO). Column (2) includes an indicator for whether there was a replacement and the replaced founder had a title below CXO (i.e., VP). Columns (3) and (4) similarly compare replacements, here distinguished by whether the replaced founder leaves or stays after being replaced (i.e., “separating” vs. “accommodating”). The main variable in Column (3) is set to one only for founders who were replaced and left the firm, while the independent variable in Column (4) corresponds to founders who were replaced yet stayed at the firm. “Controls?” indicates the inclusion of all the controls reported and defined in Table 9. Robust standard errors are in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. Next, we compared the effect of replacements where the founder stays at the startup (i.e., “accommodating” replacements; Hellmann and Puri 2002) as opposed to leaving (“separating” replacements). As mentioned, above we collected career histories for 1,322 of the 1,999 replaced founders. These data allow us to conclude whether a replaced founder stayed with the company or, if not, how long after the replacement they departed. As noted above, it could be that that “accommodating” replacements are be more beneficial as the replaced founder’s human capital is not lost; rather, the firm’s total expertise is augmented by the arrival of the replacement executive. Moreover, an accommodating replacement may reflect less dissatisfaction with the founder’s performance than if s/he was forced out of the company (although we cannot cleanly distinguish involuntary from voluntary separation in our data). By contrast, following “separating” replacements bitterness may arise among founders if they were forced out, leading them to hire away key employees (who have allegiance to the deposed founder) at a new or existing rival. However, the estimates in Columns (3) and (4) of Table 10 suggest that the positive impact of founder replacement on startup performance is more evident among founders who leave the firm.26 This may be because a departed founder cannot cause conflict or undermine a replacement as is possible if the founder remains at the firm in a possibly-undesirable role. Although our data does not allow us to cleanly adjudicate between voluntary and involuntary replacement, this result may indicate that founders who are replaced yet accommodated with a different role can be disruptive to the forward progress of the startup. It also reinforces the notion that founder replacement is a key aspect of “professionalization” led by venture capitalist investors. 5. Robustness and Identification Assumptions 5.1 Nature of non-compete changes The instrumental variable regression exploits the staggered changes in 14 states, some of which were enacted by state Supreme Court decisions and others via the legislature. Each of these has strengths and weaknesses in terms of affecting policy. Court decisions are attractive because they are generally unpredictable and apply both to future and existing contracts (Jeffers 2017), but they may also be specific to the facts of the case and not apply broadly. Laws, by contrast, are more general in nature but are often written so as to address only future contracts entered into; the enforceability of previously executed non-compete agreements may not be affected if the new law is purely forward-looking. For example, when New Hampshire began requiring in 2012 that employees be given prior notice that they will be required to sign a non-compete, this law did not immediately invalidate all prior non-compete agreements in which the worker had not been given notice. The forward-looking nature of many laws is less of a problem when the aim of the law is to strengthen the enforceability of non-compete agreements. Firms can simply require their employees to sign updated employment contracts, at least where continued employment suffices as consideration, as the effective date will fall under the auspices of the new law.27 Indeed, following the passage of the 2010 Georgia non-compete law, Atlanta-based employment attorney Benjamin Fink of Berman Fink Van Horn recalled, “[Law f]irms definitely issued alerts when the new law went into effect and many employers revised their employment and restrictive covenant agreements to take advantage of the law” (Fink 2017). Doing so would only be rational, especially given that in most states, including Georgia, the only consideration required for an existing employee to sign a new non-compete is to remain in their existing job. By contrast, in states in which the law weakened the enforceability of non-compete agreements, firms would want to avoid updating their employment agreements so that existing employees would still be bound under the previous provisions. Thus in New Hampshire and Oregon, chances are that only newly hired employees would be affected by the weakened law, which may not have as strong of an effect as if enforceability were strengthened by a new law, or if the court had issued a ruling. Accordingly, in the first three columns of Table 11, we repeat the main IV regressions for the likelihood of a positive exit while omitting these two states. Results are similar. Table 11 Robustness tests    Omit law-based weakening  Omit Texas  Omit Colorado  Omit Illinois  Omit Georgia     OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS     (1)  (2)  (3)  (4)  (5)  (6)  (7)  (8)  (9)  (10)  (11)  (12)  (13)  (14)  (15)  Founder replaced  –0.0350     0.282***  –0.0198     0.227*  –0.0282     0.301***  –0.0393     0.244**  –0.0376     0.222**     (0.0301)     (0.103)  (0.0478)     (0.138)  (0.0341)     (0.113)  (0.0345)     (0.107)  (0.0304)     (0.112)  Increased enforceability     –1.265***        –0.933***        –1.267***        –1.331***        –1.348***           (0.204)        (0.217)        (0.231)        (0.224)        (0.212)     Constant  0.0447  –1.287**  –0.125*  0.238  –1.932***  –0.164*  0.300  –1.412**  –0.0792  0.260**  –0.940*  –0.182**  0.0898  –1.066*  –0.102     (0.109)  (0.520)  (0.0738)  (0.188)  (0.646)  (0.0909)  (0.174)  (0.587)  (0.0790)  (0.101)  (0.554)  (0.0775)  (0.152)  (0.562)  (0.0759)  Observations  1217  1217  1217  698  698  698  975  975  975  1022  1022  1022  1006  1006  1006  $$R^2$$  0.0453  0.207  .  0.0592  0.257  .  0.0358  0.206  .  0.0511  0.213  .  0.0336  0.225  .  1st stage F-stat     38.52        18.58        29.99        35.26        40.31     Controls?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Financing year FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Round # FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y     Omit law-based weakening  Omit Texas  Omit Colorado  Omit Illinois  Omit Georgia     OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS     (1)  (2)  (3)  (4)  (5)  (6)  (7)  (8)  (9)  (10)  (11)  (12)  (13)  (14)  (15)  Founder replaced  –0.0350     0.282***  –0.0198     0.227*  –0.0282     0.301***  –0.0393     0.244**  –0.0376     0.222**     (0.0301)     (0.103)  (0.0478)     (0.138)  (0.0341)     (0.113)  (0.0345)     (0.107)  (0.0304)     (0.112)  Increased enforceability     –1.265***        –0.933***        –1.267***        –1.331***        –1.348***           (0.204)        (0.217)        (0.231)        (0.224)        (0.212)     Constant  0.0447  –1.287**  –0.125*  0.238  –1.932***  –0.164*  0.300  –1.412**  –0.0792  0.260**  –0.940*  –0.182**  0.0898  –1.066*  –0.102     (0.109)  (0.520)  (0.0738)  (0.188)  (0.646)  (0.0909)  (0.174)  (0.587)  (0.0790)  (0.101)  (0.554)  (0.0775)  (0.152)  (0.562)  (0.0759)  Observations  1217  1217  1217  698  698  698  975  975  975  1022  1022  1022  1006  1006  1006  $$R^2$$  0.0453  0.207  .  0.0592  0.257  .  0.0358  0.206  .  0.0511  0.213  .  0.0336  0.225  .  1st stage F-stat     38.52        18.58        29.99        35.26        40.31     Controls?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Financing year FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Round # FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  The table reports OLS and 2SLS estimates for founder replacement and entrepreneurial firm outcomes. The unit of observation is a startup headquartered in one of these states and first financed before the non-compete changes. The sample of entrepreneurial firms is described in Section 3. Triads of columns inclue the OLS, first-stage, and 2SLS estimates. Columns (1)–(3) omit states in which the legislature enacted a law that weakened the enforceability of non-compete agreements, which may have less effect than other changes as described in section 3.1. Columns (4)–(15) conduct a series of “leave one out” tests by omitting each of the largest states in our sample: Texas, Colorado, Illinois, and Georgia. “Founder replaced” is one if a financing had at least one founder replaced on the executive team. Controls and fixed effects are as defined in Tables 9. Robust standard errors are reported in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. 5.2 Single-state dependence Another question is whether the results depend entirely on the inclusion on any one of those states in particular. The remaining columns of Table 11 exclude in turn each of the largest treated states: Texas, Colorado, Illinois, and Georgia.28 These leave-one-out estimates are quantitatively and qualitatively similar. Thus it does not appear that one state is driving the main results. The results in the instrumental variables analysis are also robust to alternative definitions. Modifying the exit outcome dependent variable window from five years to two, three or four has no major impact on results (not reported, but available from the authors). The relationship between replacement and exit rates is stronger for shorter windows to exit. 5.3 Temporal separation of treated and control startups Another potential concern is that the inclusion of firms that exited or had a founder replaced many years before the law change in treated states might bias the estimates because there exist no contemporaneous treated startups. In particular, one might worry about the introduction of control firms that operated many years before the treated firms. In a series of unreported analyses, we limit the temporal distance from treated startups for this group of control startups. Specifically, for each VC that has a treated firm, we censor the control firms to 5 - 10 years before the earliest treated firm. Results (available from the authors) are robust. Thus we believe that the results are not driven by the inclusion of very early startups. 5.4 Exclusion restriction One might be concerned that shifts in the enforceability of non-compete agreements might affect venture outcomes. The literature on non-compete agreements does not address this possibility empirically, instead focusing on how such contracts affect the founding of new firms and their early growth (see Stuart and Sorenson 2003; Samila and Sorenson 2011; Starr, Balasubramanian, and Sakakibara 2015). Still, it is possible that non-compete agreements might affect venture outcomes either by affecting the market for talent, as described above, or for startups themselves (i.e., the acquisition market). To the latter point, Younge, Tong, and Fleming (2015) show evidence that enforceable non-compete agreements fuel the acquisition market for startups—presumably because it is easier to retain employees post-acquisition. If true, this would work against our finding. To the former point, the effect of non-compete agreements on hiring by startups is ambiguous. If non-compete agreements are unenforceable then startups can more easily hire workers away from established companies. But by the same token, it is easier for established companies to poach talent from startups if they cannot use non-compete agreements. Absent such evidence, we investigated the relationship between labor market fluidity and the success of venture-backed startup companies. We first check whether changes in non-compete enforceability correlate with overall performance of VC-backed firms, not just those in our IV sample. In Table A3 (see the Online Appendix), we regress state-level liquidity outcomes for venture-backed startups on the law change variable in our specification. Negative binomial analysis of the counts of IPOs and acquisitions given the number of active startups in the previous year, we find that performance correlates negatively with non-compete enforceability, but the coefficients are statistically insignificant and the implied marginal effects are small. Next, we check whether non-compete agreements facilitate venture outcomes by enabling hiring growth (again, the effect is theoretically ambiguous29). We investigate this question by merging the National Establishment Time-Series (NETS) data set, which contains employment data from Dun & Bradstreet, to firms in the sample (match rate of 62%). Table A4 in the Online Appendix resembles that of our above IV except that the endogenous variable is not founder replacement but rather a variable equal to one if the startup saw an increase in overall employment in the current year. We see the expected positive correlation between increased employment and startup success in a naive regression, but the first-stage using increase/decrease in the enforceability of non-compete agreements goes in the wrong direction and the $$F$$-statistic is small. Although the sign becomes negative in the second stage, this coefficient is very imprecisely estimated. The weakness of this result is compatible with our claim that the effect of non-compete agreements on venture outcomes is primarily through executive-level replacement as opposed to hiring more broadly. Although we cannot prove the exclusion restriction, we would have expected Table A4 to present very different results if the alternative labor-market fluidity channel were responsible for our claimed results. 6. Discussion and Conclusion This paper draws a causal link between founder replacement and startup performance. Using data on VC-backed startups in the U.S. founded from 1995 to 2008, we show that although it may appear that replacing founders hurts startup performance, this is due to selection. We introduce exogenous variation in the ability of investors to find qualified replacements by exploiting changes in the enforceability of employee non-compete agreements in 14 states. Non-compete agreements make it more difficult to hire talent, especially among the sort of established-company executives who would be attractive replacements for founders. Instrumenting our regressions reverses the result of the naive regression, indicating that founder replacement boosts the performance of startups. We find moreover that the most consequential replacements are of founders who hold CXO-level titles. Further, the positive impact of replacement appears to be stronger in “separating” replacements, that is, when founders subsequently leave the company. Taken together, these results paint a picture of activist investors “professionalizing” the nascent firm. We most directly build on four papers that explore founder replacement, three using detailed survey data from samples of 50–200 firms (Hellmann and Puri 2002; Wasserman 2003; Kaplan, Sensoy, and Strömberg 2009) and one using register data from Denmark (Chen and Thompson 2015). Our results particularly echo Hellmann and Puri’s (2002) notion that VCs “professionalize” their portfolio companies, adding a causal link. Our results complement those of Bernstein, Giroud, and Townsend (2016) and Chemmanur, Krishnan, and Nancy (2011), who have sought causal evidence regarding whether investors provide “more than money” by monitoring the progress of their portfolio firms. Although Gorman and Sahlman (1986) reveal areas in which investors spend time, we do not know which of these activities create real value. This study shows that the replacement of executives by investors is a key mechanism by which investors improve the performance of their portfolio companies. More generally, we contribute to a perennial debate in the venture capital literature regarding the value of the VC firm and partner (Ewens and Rhodes-Kropf 2015; Hellmann and Puri 2002). To date, value added by investors has primarily been found at the point of investment selection or the monitoring of firms as they grow. Given that the majority of entrepreneurial firms fail, establishing that investors can value by replacing founders represents a novel contribution. Our work is also related to the “horse-vs-jockey” debate in venture capital. Among firms that completed an IPO, Kaplan, Sensoy, and Strömberg (2009) found substantial replacement of CEOs. We likewise find a connection between founder replacement and subsequent liquidity events, but in a large sample of firms with a range of exit outcomes. Our findings suggest that investors find it productive to replace the “jockey” when they believe the underlying “horse” to be of good stock. Finally, our results speak to the tension between maintaining a founder-friendly reputation and optimizing for the performance of the current portfolio. Entrepreneurs care about their expected financial return but also about keeping their jobs. Investors’ aggressive replacement of founders may optimize the performance of the current portfolio, as our results suggest. But developing a reputation as having little patience with founders could also scare off founders—including some of the most highly able founders—who insist on remaining in control of their ventures. Although we do not measure the impact of maintaining a founder-friendly reputation on the ability to attract future entrepreneurs, and suspect that such analysis is not straightforward, our results indicate that not replacing founders is hardly costless. Future work is required to explore this tension. We recognize the support of the Kauffman Junior Faculty Fellowship. We thank John Bauer, Russell Beck, David Denis, and Matthew Rhodes-Kropf; the participants at the Duke Strategy Conference, Duke Finance department, Georgia Tech strategy department, the Northeastern entrepreneurship department; and the NBER Entrepreneurship Working Group for their comments. The VentureSource data were provided by Correlation Ventures, to which Ewens is an advisor and investor. Supplementary data can be found on The Review of Financial Studies Web site. Footnotes 1 See Hellmann and Puri (2002), Sorensen (2007), Hsu (2006), Bottazzi, Da Rin, and Hellmann (2008), and Chemmanur, Krishnan, and Nancy (2011). 2 The data were graciously provided by Correlation Ventures, a quantitative VC fund. 3 The second condition excludes firms that strictly raise capital from angel investors, hedge funds, or corporations. 4 The numbers correspond to exit outcomes from still private firms; the check was performed in April 2017 using the online search capability of both VentureSource and Pitchbook. 5 Founders, by definition, joined at the start date of the firm. 6 We lose 169 firms and 390 founders based on this rule. The firms and founders exhibit no difference in major observables studied. 7 Section A.2 in the Online Appendix has more details on this aspect of the data collection. 8 It may be that an investor remains on the board even after they stop investing in the startup, even if a new investor takes a board seat, so our count of investor-directors may be conservative. 9 The noise inherent in assigning exits dates to board seats leads to some large boards. In the raw data, fewer than 3% of boards have more than ten outside board members; however, these boards are composed of members who are listed as “former” but do not have an exit date. We truncate the outside board size at ten to remove some of this measurement error. 10 Bernstein, Giroud, and Townsend (2016) consider a dependent variable that is one if an IPO or acquisition with at least $25m exit value occurs. Our results are robust to measures of one to three times the exit value to total capital raised. 11 If an acquisition value is unreported, Puri and Zarutskie (2012) suggest that it is small. 12 The results are robust to using the median of the 6- to 9-month market capitalization of firms that had an IPO to account for the lockup period. 13 The financing year is excluded because we have one observation per startup and no event to use for selecting a financing year. 14 In unreported results, we note a strong reduced-form correlation between founder replacement and the number of acquisitions within the same industry two years prior. The two-year lag stems from a “golden handcuffs” contract commonly employed by acquiring firms for the acquired firm’s executive teams. These contracts often involve two- to four-year vesting or bonuses for the executives of acquired firms. Although the stock options of the executives in the target company fully vest on the change of control, incentives are typically added to retain key personnel beyond the acquisition, including large cash-based incentives which are evaluated no later than two years after the acquisition. Because two-year lagged acquisitions might correlate with the current exit market (e.g., merger waves), we do not use this as an instrument. 15 For further details, see Grant and Steele (1996). 16 “Blue-pencil” differs from the “red-pencil” reformation in WI in that blue-pencil allows a judge not just to strike but to rewrite objectionable parts of the contract. For example, if the non-compete is written for a duration of five years, under blue-pencil the judge can simple change the length to one or two years. 17 See also http://tradesecretstoday.blogspot.com/2011/03/failing-to-trust-public-process-of.html. 18 New York and New Mexico also weakened enforceability of non-compete agreements during our sample. The New York reform was specific to workers in the broadcasting industry which is not highly relevant to venture capital activity. Similarly, the reform in New Mexico was specific to physicians. Neither is included in our analysis. 19 The full political economy surrounding the change in Oregon is described in Rasses (2009). 20 The audio of the representative’s proposal of the new law is available at http://www.gencourt.state.nh.us/senateaudio/committees/2012/Commerce/HB%201270.asx 21 We repeated this exercise with population instead of the count of public firms and found even stronger evidence of home bias (though we think the number of public firms a better proxy for the availability of attractive executives). The above exercise confirms that startups are sensitive to changes in non-compete enforceability when hiring replacement executives. 22 Because we have a binary endogenous variable, the first stage is a probit estimator following Wooldridge 2010. From this, we gather the predicted probabilities, which we use as the IV. This approach has the advantage or producing first-stage predictions that are inside the unit interval and the first stage standard errors are correct. The results are qualitatively and statistically similar if each stage is a linear model. 23 The $$R^2$$ are not reported for the second stage because they are not a relevant summary statistic in the 2SLS setting. 24 The Hausman test for whether the 2SLS and OLS differ rejects the null that they are the same. If the IV is indeed valid, this is additional evidence that the replacement dummy is endogenous. 25 Our IV estimator uses the first stage predicted probability from a probit following Wooldridge (2010) so we have to run each as a separate regression. 26 Like in the case of the incoming replacement, whether the founder stays or leaves after being replaced may be determined by investor preference and founder preference. Investors may insist that founders depart upon replacement, or founders may decide to leave post-replacement even if investors try to retain them in a different role. As noted earlier, replaced founders who stay have less work experience and fewer master’s degrees but are more likely to have a PhD. 27 In all of the states in which enforceability was strengthened by the legislature—Florida, Idaho, Georgia, Arkansas, and Alabama—continued employment suffices as a consideration for a non-compete. 28 Note that the sample is different in each of these alternative specifications because dropping a treated state also leads to a loss of some VCs whose portfolios form the samples. 29 The limited evidence to date regarding the effect on startup hiring of non-compete agreements is moreover mixed. The only paper we are aware of in this vein is Starr, Balasubramanian, and Sakakibara 2015, who finds no effect of non-compete agreements on employee growth for the vast majority of startups. However, the 8% of startups that are intra-industry spinoffs may grow headcount faster when non-compete agreements are more strictly enforced, but only for the first three years. References Amornsiripanitch, N., Gompers, P. and Xuan. Y. 2015. More than money: Venture capitalists on boards. Working Paper. Beckman, C. M. 2006. The influence of founding team company affiliations on firm behavior. Academy of Management Journal  49: 741– 58. Google Scholar CrossRef Search ADS   Bernstein, S., Giroud, X. and Townsend. R. R. 2016. The impact of venture capital monitoring. Journal of Finance  71: 1591– 22. Google Scholar CrossRef Search ADS   Bottazzi, L., Da Rin, M. and Hellmann. T. 2008. Who are the active investors? Evidence from venture capital. Journal of Financial Economics  89: 488– 512. Google Scholar CrossRef Search ADS   Burton, M. D. 1995. The emergence and evolution of employment systems in high-technology firms. Working Paper, Stanford University. 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What do venture capitalists do? Journal of Business Venturing  4: 231– 48. Google Scholar CrossRef Search ADS   Grant, J. A.Jr., and Steele. T. T. 1996. Restrictive covenants: Florida returns to the original “unfair competition” approach for the 21st Century. Florida Bar Journal  70: 53. Hall, R. E., and Woodward. S. E. 2010. The burden of the nondiversifiable risk of entrepreneurship. American Economic Review  100: 1163– 94. Google Scholar CrossRef Search ADS   Hellmann, T., and Puri. M. 2002. Venture capital and the professionalization of start-up firms: Empirical evidence. Journal of Finance  57: 169– 97. Google Scholar CrossRef Search ADS   Hsu, D. H. 2006. Venture capitalists and cooperative start-up commercialization strategy. Management Science  52: 204– 19. Google Scholar CrossRef Search ADS   Hopkins, J. S. 2008. Non-compete bill passes House: House approves bill to protect trade secrets. Magicvalley.com  http://magicvalley.com/business/local/non-compete-bill-passes-house/article/_1e38184c-3d97-58a0-be2f-c4d5be4a06f4.html. Jeffers, J. 2017. The impact of restricting labor mobility on corporate investment and entrepreneurship. Working Paper. Kaplan, S. N., Sensoy, B. A. and Strömberg. P. 2009. Should investors bet on the jockey or the horse? Evidence from the evolution of firms from early business plans to public companies. Journal of Finance  64: 75– 115. Google Scholar CrossRef Search ADS   Kaplan, S. N., and Strömberg. P. 2003. Financial contracting theory meets the real world: An empirical analysis of venture capital contracts. Review of Economic Studies  70: 281– 315. Google Scholar CrossRef Search ADS   Malsberger, B. M., Brock, S. M. and Pedowitz. A. H. 2016. Covenants not to compete: A state-by-state survey , 10th ed. Arlington, VA: Bloomberg BNA. Marx, M. 2011. The firm strikes back non-compete agreements and the mobility of technical professionals. American Sociological Review  76: 695– 712. Google Scholar CrossRef Search ADS   Marx, M., Strumsky, D. and Fleming. L. 2009. Mobility, skills, and the Michigan non-compete experiment. Management Science  55: 875– 89. Google Scholar CrossRef Search ADS   Puri, M., and Zarutskie. R. 2012. On the life cycle dynamics of venture-capital-and non-venture-capital-financed firms. Journal of Finance  67: 2247– 93. Google Scholar CrossRef Search ADS   Rasses, M. I. 2009. Explaining the outlier: Oregon’s new non-compete agreement law and the broadcasting industry. University of Pennsylvania Journal of Business Law  11: 447– 73. Samila, S., and Sorenson. O. 2011. Noncompete covenants: Incentives to innovate or impediments to growth. Management Science  57: 425– 38. Google Scholar CrossRef Search ADS   Sorensen, M. 2007. How smart is smart money? A two-sided matching model of Venture Capital. Journal of Finance  62: 2725– 62. Google Scholar CrossRef Search ADS   Starr, E. P., Balasubramanian, N. and Sakakibara. M. 2015. Screening spinouts? How noncompete enforceability affects the creation, growth, and survival of new firms. Working Paper, US Census Bureau Center for Economic Studies. Google Scholar CrossRef Search ADS   Stock, J. H., and Yogo. M. 2005. Testing for weak instruments in linear IV regression. Identification and inference for econometric models . Ed. Andrews, D. W. K. pp. 80– 108. New York: Cambridge University Press. Stuart, T. E., and Sorenson. O. 2003. Liquidity events and the geographic distribution of entrepreneurial activity. Administrative Science Quarterly  48: 175– 201. Google Scholar CrossRef Search ADS   Wasserman, N. 2003. Founder-CEO succession and the paradox of entrepreneurial success. Organization Science  14: 149– 72. Google Scholar CrossRef Search ADS   Weisbach, M. S. 1988. Outside directors and CEO turnover. Journal of Financial Economics  20: 431– 60. Google Scholar CrossRef Search ADS   Wooldridge, J. M. 2010. Econometric analysis of cross section and panel data . Cambridge: MIT press. Younge, K. A., Tong, T. W. and Fleming. L. 2015. How anticipated employee mobility affects acquisition likelihood: Evidence from a natural experiment. Strategic Management Journal  36: 686– 708. Google Scholar CrossRef Search ADS   © The Author 2017. Published by Oxford University Press on behalf of The Society for Financial Studies. All rights reserved. For Permissions, please e-mail: journals.permissions@oup.com http://www.deepdyve.com/assets/images/DeepDyve-Logo-lg.png The Review of Financial Studies Oxford University Press

Founder Replacement and Startup Performance

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© The Author 2017. Published by Oxford University Press on behalf of The Society for Financial Studies. All rights reserved. For Permissions, please e-mail: journals.permissions@oup.com
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Abstract

Abstract We provide causal evidence that venture capitalists (VCs) improve the performance of their portfolio companies by replacing founders. Using a database of venture capital financings augmented with hand-collected founder turnover events, we exploit shocks to the supply of outside executives via 14 states’ changes to non-compete laws from 1995 to 2016. Naive regressions of startup performance on replacement suggest a negative correlation that may reflect negative selection. Indeed, instrumented regressions reverse the sign of this effect, suggesting that founder replacement instead improves performance. The evidence points to the replacement of founders as a specific mechanism by which VCs add value. Received January 16, 2016; editorial decision August 3, 2017 by Editor Francesca Cornelli. Authors have furnished an Internet Appendix, which is available on the Oxford University Press Web Site next to the link to the final published paper online. It is well accepted that venture capital (VC) is a “hits” business. In a sample of over 22,000 VC-funded startups founded between 1987 and 2008, 75% had a liquidation value of zero while 0.39% had an exit value of $500 million or greater (Hall and Woodward 2010). Research indicates that returns are enhanced by investor skills, which one might group by (1) initial selection of investment targets and (2) post-investment intervention.1 Recently, scholars have turned their attention to the question of whether post-investment intervention by “activist” investors truly improves outcomes for portfolio companies (Bottazzi, Da Rin, and Hellmann 2008). Chemmanur, Krishnan, and Nancy (2011) use restricted-access Census data to show that startups ineligible for Small Business Administration support achieve greater total factor productivity after raising VC, suggesting that investors provide more than just capital. Bernstein, Giroud, and Townsend (2016) similarly find that VC-backed firms are more likely to achieve liquidity events once their investors are able to visit via a nonstop flight. But neither paper identifies specific actions undertaken by investors, leaving open the question of exactly how activist investors add value. Gorman and Sahlman (1986) list three nonfinancial areas, where investors spend time ostensibly in the interest of improving performance. First, VCs assist with strategic and operational planning. In support of the notion that investors influence strategic direction, Hsu (2006) finds that VC-backed ventures are more likely to adopt cooperative commercialization strategies. But whether such assistance improves outcomes remains in question, especially as Kaplan, Sensoy, and Strömberg (2009) see little change in business plans among VC-backed startups that achieve initial public offerings (IPOs). Second, investors may make introductions to customers that facilitate sales and drive revenue growth. The plausibility of this mechanism is underscored by Chemmanur, Krishnan, and Nancy (2011), who suggest that TFP gains for VC-backed startups are largely coincident with increased sales. But customer introductions are difficult to observe empirically, so constructing a clean test of this mechanism is difficult. The third category—recruiting managers—is easier to observe; indeed, VCs are known to play a role in recruiting (see Amornsiripanitch, Gompers, and Xuan 2015). Nevertheless, it is not straightforward to conclude a direct link between such actions and performance. Recruiting can be purely additive, such as when an investor brings a vice president of marketing to an early-stage company that previously did not have one, or it can involve replacing existing personnel. For example, the relevant survey question in Bottazzi, Da Rin, and Hellmann (2008) asks, “Has your firm been involved in recruiting senior management for this company?” which could be of either type. Additive recruiting is unlikely to be controversial whereas founders may resist being replaced. At least four studies have examined founder replacement. In a survey of 170 Silicon Valley based startups, Hellmann and Puri (2002) find that VC-backed ventures are more likely than others to replace the original founder-CEO (and execute such replacements earlier in the life of a startup). They attribute founder replacement to a process of “professionalization” whereby the adolescent venture becomes a more mature company. Consistent with this view, and also using survey data from approximately 200 (nationwide) companies, Wasserman (2003) finds that founder replacement coincides with milestones in the development of a startup such as completing product development or raising a new round of financing. Wasserman also finds that the likelihood of a founder being replaced is increasing in the number of outsiders on the board of directors, suggesting that investors may replace founders proactively. Kaplan, Sensoy, and Strömberg (2009) find that 42% of founders among 50 VC-backed startups that completed an IPO were replaced, suggesting that such “professionalization” may be associated with positive venture outcomes. Although these studies provide a wealth of insight into the phenomenon of founder replacement, including reasons for replacement and the subsequent disposition of the replaced founder, they do not formally test the connection between founder replacement and venture outcomes. Chen and Thompson (2015) attempt to draw a connection between founder replacement and performance by merging the Danish register of 4,172 of new businesses with the country’s register data. They note that startups experiencing founder replacement were more likely to fail, although firms that had a replacement and nonetheless survived grew faster. However, they stop short of making causal claims. Drawing inferences regarding the impact of founder replacement on performance is challenging because founder replacement is endogenous. Founders may decide to leave the firm voluntarily, either because they see their startup’s prospects as dim or because they are “serial” entrepreneurs who prefer to be involved only in the early stages and then depart to start another venture. Replacement may instead be involuntary. Control rights afforded investors via contracts as well as voting rights on the board of directors enable investors to force founders to relinquish their role. They may replace a founder when the business is struggling—as Chen and Thompson’s (2015) data suggest—but they may also elect to replace when the startup is growing quickly yet the investors doubt the founder’s ability to scale up the company (as Wasserman 2003 suggests). In addition, the quality of the person hired to replace the founder may be endogenous. It may be harder to attract strong executives to struggling startups. Moreover, the ability to attract top talent may depend on the quality of the investors and their networks (Amornsiripanitch, Gompers, and Xuan 2015). It might seem self-evident that replacing founders would help firm performance. If investors are rational and add value by monitoring the firm (Bottazzi, Da Rin, and Hellmann 2008; Chemmanur, Krishnan, and Nancy 2011; Bernstein, Giroud, and Townsend 2016), then they should not replace founders unless doing so is beneficial. However, if investors think that they are better informed than the founders but are often incorrect, replacement could be generally detrimental. For example, investors may underestimate the influence of a founder and thus the negative impact of their departure. Moreover, even if investors are correct that the founder should leave the company, removing a founder may have unintended negative consequences such as if loyal-to-the-founder employees become disenchanted and leave. (They may even be recruited away by the deposed founder.) Investors sensitive to that risk may instead try to retain the replaced founder in a different role, but the founder may thwart this plan by refusing to stay once replaced. To address the issue of the effect of founder replacement on firm outcomes, we construct a novel database of VC-backed founders and their replacements. The data builds on the VentureSource repository of entrepreneurial firms, financings, investors and executives. A multi-pronged data collection and cleaning augmented VentureSource by identifying founders as well as replacements of founders (in executive roles, i.e., VP and above) at VC-backed firms founded between 1995 and 2008. Our final sample includes 11,929 firms and 19,830 founders. Some 15% of firms have at least one founder replacement in our sample period, almost 40% of whom appear to stay at the startup after they are replaced. The first major question that we ask is whether these replacements correlate with startup firm exit outcomes. Naive regressions show a negative correlation between founder replacement and liquidity events. Similar to Wasserman (2003), we find that founder replacement is more likely to occur following a new round of financing as well as when the board contains more investors. But as argued above, even if VCs play a primary role in replacing founders the negative correlation between replacement and subsequent performance could be explained by selection if investors choose to replace a founder when a startup is in trouble or because a highly qualified replacement is hard to find (including when founders relinquish their role voluntarily). We then instrument for founder replacement using a plausibly exogenous shock to the supply of executives who might serve as suitable replacements: changes in the enforceability of employee non-compete agreements. Non-compete agreements have frequently been shown to restrict the mobility of workers, especially technologists and executives in the sorts of high-potential industries VCs tend to invest in (Marx, Strumsky, and Fleming 2009; Marx 2011; Garmaise 2011). Thus the ability of an investor to attract a qualified replacement may depend on the extent to which non-compete agreements are enforceable. The large-scale data on founder replacement we build off of VentureSource enables us to assess the impact of non-compete agreements by exploiting staggered changes in 14 states, some of which tightened enforceability while others loosened enforceability. Founders are less (more) likely to be replaced when non-compete enforceability has been strengthened (weakened). The larger data set of founder replacements we collected enables us to test the effect of these employment contracts on replacement rates and subsequent venture performance. Instrumenting for founder replacement with these policy changes shows that replacement increases the likelihood of achieving a high-quality liquidity event such as an IPO or attractive acquisition. The instrumented finding reverses the correlation found in the naive cross-sectional analysis. Decomposition of the instrumented results reveals which types of replacements have the greatest impact. Replacing founders who hold CXO roles, such as Chief Executive Officer (CEO) and Chief Financial Officer (CFO), is more consequential than replacing founders in lower roles. Interestingly, replacement appears to help more when replaced founders leave the startup after relinquishing their role. Taken together, these findings point to the role of venture capitalists in professionalizing their portfolio companies by replacing founders with more experienced executives. Replacement is more common following a round of funding and when investors hold more board power, and replacement contributes more to positive venture outcomes when CXO-level founders leave the company. Insofar as venture capitalists play an important role in both the decision to replace founders and identify their replacements, the positive causal effects we find establish a mechanism by which VCs add value to their portfolio firms. In doing so, we extend the literature on how venture capitalists add value, which has previously demonstrated some causal effect of VC activism on performance but has left open the question of how this value is added. 1. Data The objective of the data collection discussed here and in more detail in the Online Appendix is to create a representative sample of VC-backed founders and the incidence of their replacement. To our knowledge, such a database with broad coverage does not exist, so we assembled one using several different sources of information. To start, we collected the set of VC-backed startups founded from 1995 to 2008 using VentureSource. VentureSource is a database of venture capital transactions, entrepreneurial firms, company executives, investments and outcomes provided by Dow Jones.2 VentureSource is however less reliable in capturing information about founders as startups are not required to report exhaustive founder data. Rather, VentureSource gathers information on founders from the startups themselves as well as third-party sources. We addressed these limitations with several data collection efforts. VentureSource has incomplete coverage of founders either because some firms have no founders identified or similarly, some of the executives of the firm are incorrectly labeled as nonfounders. We addressed these issues by starting with the data from Ewens and Fons-Rosen 2015 firms along with an extensive search for missing founders using LinkedIn, Crunchbase, company Web sites, and CapitalIQ. For the 2,159 firms in which VentureSource listed no founders, we found 3,516 missing founders. Next, even if a startup has one founder it may be that other executives listed in VentureSource for that firm are missing the founder label. To begin, for all 6,219 firms with just one founder, a research assistant examined all the other executives using the Web sites mentioned above to determine whether that executive was also a founder. This process resulted in 1,226 additional founders. Several other data collection tasks were completed to try and remedy missing founders (the Online Appendix details each of these in depth). Using the steps above we found 5,259 additional founders, which raised the average founding team size from 1.6 in the raw VentureSource data to 2.15 in our final sample. This compares favorably with prior work on founding teams. Kaplan, Sensoy, and Strömberg 2009 report 1.9 founders on average in their same of 48 venture-backed companies that completed an IPO. Beckman 2006 extend the data set used by Hellmann and Puri 2002 to include all founders of the 173 Silicon-Valley-based companies collected by Burton 1995, finding 2.2 founders on average. Wasserman 2003 reports an average of 2.5 founders among a combination of 202 venture-backed and non-venture-backed startups. With the new founders collected, sample creation begins with the the set of all VC-backed entrepreneurial firms founded between 1995 and 2008. The lower bound of founding year ensures that we can collect information about replacements via all the sources discussed below, while the upper bound ensures that we have time for exits as the sample ends in April 2017. We further filter VentureSource data according to its coverage of management teams by requiring that the firm has at least one founder (90% of firms have at least one after data cleaning) and raised some capital from a traditional venture capital firm.3 We also require that the founder have a title at or above the level of vice president to ensure they have a major operating role at the firm. The final sample has 19,830 founders of 11,929 entrepreneurial firms. Over 75% of the firms in the sample have exited by April of 2017.4Table 1 provides a summary of most of the variables used in this paper, and Table 2 provides summary statistics. Table 1 Variable description Went public  Startup completed initial public offering by end of sample (April 2017)  Acquired  Startup exited via an acquisition or merger by the end of sample with valuation at least 125% of total capital raised (April 2017). If unknown, exit value is assumed to be 25% of capital invested  Log exit value  Ln price of acquisition or merger  IPO/Acq.  Startup exited via an IPO or an acquisition. If unknown, exit value is assumed to be 25% of capital invested  Still private  Startup remains private as of the end of the sample (April 2017)  Out of business  Startup went out of business by the end of the sample (April 2017)  Year firm founded  Startup founding year, set to the year of first VC financing if unknown  Biotech  Startup industry is health care or biotechnology  Information technology  Startup industry is information technology  Year first VC  Year the startup first raised equity capital from VCs  First capital raised  Capital raised in the first first round of VC financing  Total capital raised (m)  Total capital raised by a startup across all its financing events  Capital stock  Capital raised as of each financing event  Total equity financings (all)  Total financing rounds with VC for the startup  Size of VC board  Number of board member investors as of each financing event  Age of firm  Age of entrepreneurial firm at a financing event in years since firm founding  CXO  Dummy for each of the major titles for executives: (where “X” can be E, F, T, I, or M)  Solo founder  Founder is only executive at the startup at the time of founding  Syndicate size  The number of investors in the current financing round  Profitable at financing  Startup reported profits in a given financing  Increased Enforceability  An indicator for whether a startup was in a state that had a decrease ($$-1$$) or an increase (1) in non-compete enforceability, and (0) represents no change  Founder replaced  Two executives at the startup had the same nonshared job title, and one joined later than the founding date.  Stayed  Replaced founder stayed with the company instead of leaving  Round # FEs  Financing round number fixed effects  Industry FEs  Startup industry fixed effects: “Business/Consumer/Retail,” “Healthcare,” “Information Technology” and “Other”  State FEs  State fixed effects for the headquarters of the startup  Year FEs  Financing year fixed effects  Went public  Startup completed initial public offering by end of sample (April 2017)  Acquired  Startup exited via an acquisition or merger by the end of sample with valuation at least 125% of total capital raised (April 2017). If unknown, exit value is assumed to be 25% of capital invested  Log exit value  Ln price of acquisition or merger  IPO/Acq.  Startup exited via an IPO or an acquisition. If unknown, exit value is assumed to be 25% of capital invested  Still private  Startup remains private as of the end of the sample (April 2017)  Out of business  Startup went out of business by the end of the sample (April 2017)  Year firm founded  Startup founding year, set to the year of first VC financing if unknown  Biotech  Startup industry is health care or biotechnology  Information technology  Startup industry is information technology  Year first VC  Year the startup first raised equity capital from VCs  First capital raised  Capital raised in the first first round of VC financing  Total capital raised (m)  Total capital raised by a startup across all its financing events  Capital stock  Capital raised as of each financing event  Total equity financings (all)  Total financing rounds with VC for the startup  Size of VC board  Number of board member investors as of each financing event  Age of firm  Age of entrepreneurial firm at a financing event in years since firm founding  CXO  Dummy for each of the major titles for executives: (where “X” can be E, F, T, I, or M)  Solo founder  Founder is only executive at the startup at the time of founding  Syndicate size  The number of investors in the current financing round  Profitable at financing  Startup reported profits in a given financing  Increased Enforceability  An indicator for whether a startup was in a state that had a decrease ($$-1$$) or an increase (1) in non-compete enforceability, and (0) represents no change  Founder replaced  Two executives at the startup had the same nonshared job title, and one joined later than the founding date.  Stayed  Replaced founder stayed with the company instead of leaving  Round # FEs  Financing round number fixed effects  Industry FEs  Startup industry fixed effects: “Business/Consumer/Retail,” “Healthcare,” “Information Technology” and “Other”  State FEs  State fixed effects for the headquarters of the startup  Year FEs  Financing year fixed effects  The table reports descriptions of the variables used in regression analysis. Table 2 Summary statistics    Firm characteristics     Mean  SD  Min  p25  p50  p75  Max  Firms  Acquired  0.41  0.49  0  0  0  1  1  11929  Went public  0.060  0.24  0  0  0  0  1  11929  Out of business  0.28  0.45  0  0  0  1  1  11929  Still private  0.24  0.43  0  0  0  0  1  11929  First capital raised  6.47  20.1  0.0100  1.50  3.50  6.75  1500  11929  Year firm founded  2001.0  3.82  1990  1998  2000  2004  2010  11929  Information technology  0.54  0.50  0  0  1  1  1  11929  Biotech  0.18  0.39  0  0  0  0  1  11929  California HQ  0.41  0.49  0  0  0  1  1  11929  Texas HQ  0.053  0.22  0  0  0  0  1  11929  New York HQ  0.066  0.25  0  0  0  0  1  11929  Total equity financings (all)  3.53  2.39  1  2  3  5  24  11929  Total capital raised (m)  37.6  126.4  0  5.35  16  40.8  10328.6  11929  Year first VC  2002.5  4.29  1995  1999  2001  2006  2014  11929  Founder replaced?  0.15  0.36  0  0  0  0  1  11929     Firm characteristics     Mean  SD  Min  p25  p50  p75  Max  Firms  Acquired  0.41  0.49  0  0  0  1  1  11929  Went public  0.060  0.24  0  0  0  0  1  11929  Out of business  0.28  0.45  0  0  0  1  1  11929  Still private  0.24  0.43  0  0  0  0  1  11929  First capital raised  6.47  20.1  0.0100  1.50  3.50  6.75  1500  11929  Year firm founded  2001.0  3.82  1990  1998  2000  2004  2010  11929  Information technology  0.54  0.50  0  0  1  1  1  11929  Biotech  0.18  0.39  0  0  0  0  1  11929  California HQ  0.41  0.49  0  0  0  1  1  11929  Texas HQ  0.053  0.22  0  0  0  0  1  11929  New York HQ  0.066  0.25  0  0  0  0  1  11929  Total equity financings (all)  3.53  2.39  1  2  3  5  24  11929  Total capital raised (m)  37.6  126.4  0  5.35  16  40.8  10328.6  11929  Year first VC  2002.5  4.29  1995  1999  2001  2006  2014  11929  Founder replaced?  0.15  0.36  0  0  0  0  1  11929  The table reports the summary statistics of the firms in the sample. 1.1 Identifying founder replacement Recruiting executives are one of the most commonly mentioned value-add activities observed in the literature on VC monitoring (Gorman and Sahlman 1986; Hellmann and Puri 2002; Bottazzi, Da Rin, and Hellmann 2008). Recruiting could be “additive” in that it helps to complete a nascent founding team, for example, by adding a Vice President of Marketing to a technology-focused startup. But recruiting can also take place for roles already occupied when a replacement is sought. Additive recruiting is unlikely to be controversial, whereas our interest is in the dynamics and impact of replacement. Replacement might be uncontroversial if founders are eager to relinquish their role, or it might be difficult if founders and investors differ in their view of the founders’ suitability to continue in their current role. VentureSource includes information on top-level managers, executives and investor board members. For each executive, VentureSource contains the title held at the venture-backed firm(s) where that person worked. Whenever we observe two individuals at a startup with the same title (excepting inherently joint titles such as “co-CEO”) we conclude that a replacement has occurred. We normalize job titles both by level (e.g., “VP” and “Vice President”) and by function (e.g., “Software Development” vs. “Software Engineering”), while being careful not to lump together titles at the same level and in the same function that are nonetheless distinct (e.g., “VP North American Sales” and “VP International Sales”). Since we aim to identify within-firm replacements, most of the within-firm variation in title naming is due to typography. Because we are ultimately interested in the dynamics of founder replacement, the join date for each new occupant of a given title is essential.5 Unfortunately, join dates are missing for approximately 70% of the replacement executives in VentureSource. We undertook a data collection process using company Web sites, Capital IQ, Zoominfo and public LinkedIn resumes, which typically include an online biography or resume from which the join date can be extracted or inferred. The comparison of titles across all executives identifies a potential replacement. With this list in hand, we have a smaller set of individuals for which to search for join dates. We are able to add the join date for more than 1,500 replacement executives, reducing the missing join dates to 16% of replacement executives. Founders who were replaced but for whom we do not have the join date of the executive who replaced them are dropped from the analysis as we cannot properly establish the timing of the replacement.6 For nonjoint titles for which we have join dates for all occupants, we take the join date(s) of the nonfounder occupant(s) as an indication of a founder replacement. For example, if a startup had both a founder and a nonfounder with the job titles “VP Product” and “Vice President of Product Management” with start dates of January 1, 1995 and June 5, 1997, we take June 5, 1997, as the date of the replacement. We then retain the set of these replacements where the first to hold the position was a founder of the company. One additional concern regarding our sample construction is that the firms that are out of the sample either failed or were shut down before VentureSource collected the data on replacement. Similarly, people who were associated with the company may not have made that known online. Such selection will attenuate any negative relationship between replacement and firm performance. For the question of whether replacement matters, we may have too many “good” replacements (i.e., those that are worth it and those that help). We researched twenty-five random out-of-sample firms to isolate any patterns. Sixteen of the companies appear to have failed and have not raised new VC in many years. Several of the remaining are in nontraditional VC industries such as retail and restaurants where VentureSource may have poor coverage. Overall, the sample of entrepreneurial firms for which we are confident about replacement events is representative of the typical VC-backed firm over the sample period. 1.1.1 Decomposing the nature of replacement As characteristics of the replaced founder, the incoming executive, or the replacement more generally may affect subsequent performance, we collect additional data regarding replaced founders and their incoming replacements. The above-described data collection tells us the role held by the replaced founder, and VentureSource contains a “biography string” listing previous positions. The string does not indicate the years of experience the replacement had, whether s/he had previously founded a startup, or anything regarding educational background. We also want to know what happened to the founder following that replacement as well as characteristics of the incoming executive. Using LinkedIn, we were able to capture career histories for 1,322 of the 1,999 replaced founders as well as the new, incoming managers who replaced them (a total of 2,028 executives).7 In their detailed survey data, Hellmann and Puri (2002) find that 40% of replaced founders continue at a startup in a new role, which they refer to as an “accommodating” replacement as opposed to a “separating” replacement where the replaced founder leaves the company. We classify replacements into these two categories as follows: If VentureSource lists a subsequent job for that founder at the startup, we label the replacement as “accommodating.” Even if VentureSource does not show a subsequent role for the replaced founder, we label the replacement as “accommodating” if their LinkedIn profile claims that they were employed by the firm for at least two years after the replacement date in VentureSource. This condition holds unless LinkedIn lists another job within that two-year period (in case the founder moved to an advisory role or such). The Online Appendix provides additional detail on this aspect of the data collection process. We find 38% of replacements to have been “accommodating,” rather close to the 40% reported in Hellmann and Puri (2002). Replaced founders who stay have less experience than those who leave but are more likely to have previously founded a company. They also appear somewhat more likely to have a PhD and somewhat less likely to have an MBA (Table A2 in the Online Appendix). Our analysis thus builds on Hellmann and Puri 2002 in that we are able to assess the causal effect of different types of replacement. These data also enable us to describe incoming replacement executives and compare them with the founders they replace. Among the fields captured in this data collection effort were the person’s years of work experience, whether the person had previously founded a startup, and education. Regarding education, we noted whether the person had a bachelor’s degree, master’s degree, MBA, MD, or PhD. Table 3 compares replaced founders with the new, incoming replacement managers along all of the fields we collected. The comparison suggests that replacement executives tend to have almost two years more experience than the replaced founders but are less than half as likely to have previously founded a startup. They are somewhat more likely to have an MBA and to have completed college. Replacements are more likely to have held CXO-level positions but have a CEO position. Table 3 Comparison of replaced founders and their replacements    Replaced founders  Replacements  Diff/s.e.  Years experience pre-startup  15.44  17.25  –1.803***           0.394  Number jobs on LinkedIn  4.481  5.520  –1.038***           0.126  Held CEO position  0.579  0.562  0.0176           0.0235  Past founder  0.601  0.165  0.436***           0.0206  Held CXO position  0.889  0.923  –0.0339**           0.0138  PhD  0.127  0.113  0.0143           0.0154  MD  0.0297  0.0123  0.0175**           0.00679  MBA  0.248  0.304  –0.0563***           0.0212  Master’s degree (including MBA)  0.435  0.448  –0.0127           0.0236  Bachelor’s degree  0.783  0.819  –0.0365*           0.0189  # LinkedIn connections (truncated)  297.7  307.6  –9.926           10.40  Number individuals  1,014  1,014  2,028     Replaced founders  Replacements  Diff/s.e.  Years experience pre-startup  15.44  17.25  –1.803***           0.394  Number jobs on LinkedIn  4.481  5.520  –1.038***           0.126  Held CEO position  0.579  0.562  0.0176           0.0235  Past founder  0.601  0.165  0.436***           0.0206  Held CXO position  0.889  0.923  –0.0339**           0.0138  PhD  0.127  0.113  0.0143           0.0154  MD  0.0297  0.0123  0.0175**           0.00679  MBA  0.248  0.304  –0.0563***           0.0212  Master’s degree (including MBA)  0.435  0.448  –0.0127           0.0236  Bachelor’s degree  0.783  0.819  –0.0365*           0.0189  # LinkedIn connections (truncated)  297.7  307.6  –9.926           10.40  Number individuals  1,014  1,014  2,028  We retrieved career histories for 1,322 of the 1,999 replaced founders, as well as their replacements, from LinkedIn (2,028 individuals in total). Table reports means, differences and two-sided t-statistic p-values for the replaced founders and the incoming replacement executives. All variables are measured at the time (year) of the startup’s founding. Table 1 defines the variables. Standard errors are reported in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. 1.2 Descriptives and correlates of founder replacement Before proceeding to our analysis of venture performance, we characterize founder replacement in our data. Table 4 shows the dynamics of founder replacement by financing round. As noted in the last row of Table 4, 15.1% of venture-backed firms in our sample experience a founder-replacement event (18.6% if we include those for which we cannot determine the date of the replacement). Founder replacement is less common in the first round, rises in the second round and continues well into the sixth round. Table 4 Founder replacement patterns    Round number     1  2  3  4  5  6+  Startups raising Nth round of funding  11,929  10,145  7,444  5,120  3,301  2,046  Startups achieving liquidity this round  860  941  785  598  404  499  Startups failing this round  1,510  1,257  839  531  321  421  Startups with founder replaced this round  429  599  400  229  121  131  Startups with founder replaced so far  429  1,008  1,379  1586  1,697  1,811  % startups with founder replaced this round  3.6%  5.9%  5.3%  4.5%  3.7%  6.4%  % startups with founder replaced so far  3.6%  8.4%  11.5%  13.2%  14.2%  15.1%     Round number     1  2  3  4  5  6+  Startups raising Nth round of funding  11,929  10,145  7,444  5,120  3,301  2,046  Startups achieving liquidity this round  860  941  785  598  404  499  Startups failing this round  1,510  1,257  839  531  321  421  Startups with founder replaced this round  429  599  400  229  121  131  Startups with founder replaced so far  429  1,008  1,379  1586  1,697  1,811  % startups with founder replaced this round  3.6%  5.9%  5.3%  4.5%  3.7%  6.4%  % startups with founder replaced so far  3.6%  8.4%  11.5%  13.2%  14.2%  15.1%  The table reports replacement rates across financing round sequence. Sample includes entrepreneurial firms tracked by VentureSource that satisfy the sample conditions in Section 1. The number of startups receiving an $$N$$th round of funding is lower than the number who received funding in a prior round, less exits, because some firms continue as private entities without raising subsequent financing. Next, we adopt a hazard specification of a particular founder being replaced as the data are right-censored and the phenomenon is observed on a continuous basis. Although we observe the exact date of a replacement, we create quarterly spells (results are robust to the use of monthly spells). We first account for characteristics of the founder, including whether that founder had a CXO title and whether there were any cofounders. We then track financing, including new rounds of funding, the overall level of funding to date, and whether the startup was profitable as of that round of financing. Recent financing rounds and the overall level of investment may proxy for the power of investors to replace founders. To further assess the role of investor power in replacing founders, we examine the number of directors who are investors. The board is explicitly tasked with hiring and firing the CEO and can exert significant influence over the hiring and firing of other executives. Similar studies of public firm boards, such as Weisbach 1988, show a direct connection between board size and investor power. Furthermore, the VC-backed entrepreneurial firm has a board of directors comprised of three different agents: independent observers, investors, and executives (see Kaplan and Strömberg 2003 for details). Analyzing board investor power requires the number of VCs who are directors in each round. VentureSource lists current/former board members, but dates of service are often missing. We identify an investor’s joining the board by their first investment in which either they are identified as the “lead”—or if they never have a lead position, their first investment in the firm. Identifying their exit from the board is more challenging as most will retain their position, although some early-stage VCs leave a board as the startup approaches an IPO. We date exits by the round where a known investor stops participating in financing events and a new investor takes a board seat.8 Finally, we create a dichotomous variable set to one if the board size is above the median outside board size (results are qualitatively similar with the continuous measure).9 Table 5 reports factors associated with the hazard of founder replacement. We find that the hazard of replacement is increasing not only in a new round of financing—whether in that quarter, as shown, or (in unreported results) during the previous two quarters —but also in the total amount of funding raised so far and in the number of investors on the board of directors. Consistent with Wasserman 2003, this suggests that investors indeed play a role in founder replacement, perhaps as a condition of a new round of funding or as part of their governance responsibilities as members of the board of directors. However, profitability is not associated with replacement in a statistically significant fashion. Founders holding a CXO role are more likely to be replaced than others. Table 5 Correlates of founder replacement    (1)  (2)  (3)  (4)  (5)  New financing round this quarter  0.265***  0.424***  0.316***  0.172**  0.264***     (0.0519)  (0.126)  (0.114)  (0.0678)  (0.0519)  Profitable at prior financing  0.0604  0.184  –0.404  0.116  0.0872     (0.109)  (0.182)  (0.342)  (0.156)  (0.109)  log capital stock at prior financing  0.153***  0.206***  0.104*  0.167***  0.151***     (0.0254)  (0.0587)  (0.0595)  (0.0337)  (0.0255)  Size of VC board  0.114***  0.169***  0.0567  0.115***  0.112***     (0.0192)  (0.0467)  (0.0459)  (0.0253)  (0.0194)  Founder held CXO role  0.264***  0.427***  0.355***  0.174***  0.266***     (0.0534)  (0.130)  (0.131)  (0.0669)  (0.0533)  Solo founder  0.0814  0.0449  –0.0477  0.202***  0.0985*     (0.0526)  (0.119)  (0.117)  (0.0706)  (0.0535)  Observations  411266  91715  79738  225869  411266  Log likelihood  –17067.4  –2542.6  –2570.7  –9643.8  –17061.3  Number of startups  11817  2941  2164  6334  11817  Industries  All  Consumer  Health care  IT  All  Industry FEs  N  N  N  N  Y     (1)  (2)  (3)  (4)  (5)  New financing round this quarter  0.265***  0.424***  0.316***  0.172**  0.264***     (0.0519)  (0.126)  (0.114)  (0.0678)  (0.0519)  Profitable at prior financing  0.0604  0.184  –0.404  0.116  0.0872     (0.109)  (0.182)  (0.342)  (0.156)  (0.109)  log capital stock at prior financing  0.153***  0.206***  0.104*  0.167***  0.151***     (0.0254)  (0.0587)  (0.0595)  (0.0337)  (0.0255)  Size of VC board  0.114***  0.169***  0.0567  0.115***  0.112***     (0.0192)  (0.0467)  (0.0459)  (0.0253)  (0.0194)  Founder held CXO role  0.264***  0.427***  0.355***  0.174***  0.266***     (0.0534)  (0.130)  (0.131)  (0.0669)  (0.0533)  Solo founder  0.0814  0.0449  –0.0477  0.202***  0.0985*     (0.0526)  (0.119)  (0.117)  (0.0706)  (0.0535)  Observations  411266  91715  79738  225869  411266  Log likelihood  –17067.4  –2542.6  –2570.7  –9643.8  –17061.3  Number of startups  11817  2941  2164  6334  11817  Industries  All  Consumer  Health care  IT  All  Industry FEs  N  N  N  N  Y  The table presents a hazard analysis of founder replacement. Observations are firm-founder-quarter triads, with failure defined as the founder being replaced in that quarter. Variables are as defined in Table 1. Columns 2–4 investigate individual industries. Standard errors are reported in parentheses and clustered at the startup level. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. We also see some differences among industries. Health care in particular differs from other industries in that neither the level of funding to date nor the size of the board predicts replacement. Also, solo founders are somewhat more likely to be replaced in IT startups, and more generally when industry fixed effects are included. 2. Does Founder Replacement Affect Performance? As noted above, Bernstein, Giroud, and Townsend (2016) establish a causal connection between investor activism and IPO/acquisition outcomes but do not demonstrate specific mechanisms as to how these benefits are achieved. Although prior work has shown that investors indeed replace founders of their portfolio companies (Kaplan, Sensoy, and Strömberg 2009; Hellmann and Puri 2002; Wasserman 2003), the only paper to draw a connection between founder replacement and venture outcomes is Chen and Thompson (2015), who stop short of claiming causality. To study the impact of founder replacement on firm outcomes, we measure the ultimate success of the firm. We extend the commonly used outcome variable—an IPO—to two more general measures of success. The first dependent variable is set to one for a portfolio that achieves an IPO or an attractive acquisition that exceeds 125% of total capital raised.10 An unattractive acquisition or failure of the firm both set the dependent variable to zero.11 Although 10% of firms achieve an IPO, some 20% of firms in our sample achieve a successful exit. The second outcome variable is the log of the observed exit valuation, which is set to 25% of capital raised if the startup failed. Exit valuation for nonfailures is either the final acquisition valuation or IPO market capitalization at the date of the offering.12 For firms without a reported exit valuation – predominantly acquired firms that were likely acquired for relatively low valuations – we treat the exit as a failure. This is not a strong assumption because the dummy variable above effectively does the same; moreover, Puri and Zarutskie (2012) show that many acquisitions are in fact hidden failures. These two dependent variables have a correlation of over 60%, however, the exit valuation provides an alternative continuous measure of success. The empirical model ties the founder replacement to outcome $$Y_{i}$$:   \begin{equation} \textrm{Y}_{i} = \rho_0 + \rho_1 R_{i} + \rho_2 X_{i} + \gamma_t + \phi_{\it State(i)} + v_{i}. \end{equation} (1) Here $$X_{i}$$ contains entrepreneurial firm characteristics such as firm age, syndicate size, profitability, and total capital raised. Time-varying measures are calculated either at each financing event, each quarter or at the last financing event prior to the time of the law changes we use in the instrumental variable analysis. It will also capture fixed effects for founding year, stage (round number) and industry. State fixed effects are captured with $$\phi_{\it State(i)}$$ and $$\gamma_t$$ represents financing year fixed effects. The variable $$R_{i}$$ indicates whether a founder was replaced. The unit of observation is an entrepreneurial firm. Table 6 estimates this equation on the full sample of startups as described above.13 As is visible from Column 1, there is a strong negative correlation between founder replacement and favorable outcomes. Column 2 repeats the exercise for CXO replacements only. Columns 3 and 4 consider the log exit valuation defined above and thus measures the size of a liquidity event. The results are similar to those in the first two columns, suggesting again that startups where a founder was replaced tend to underperform on average. Table 6 Full sample exit outcomes and founder replacement    IPO/Acq.?  log exit value     (1)  (2)  (3)  (4)  Founder replaced?  –0.0472**     –0.211**        (0.0198)     (0.0881)     Founder-CXO replaced?     –0.0577***     –0.289***        (0.0170)     (0.0773)  Constant  0.302***  0.300***  –0.475  –0.486     (0.0551)  (0.0553)  (0.407)  (0.408)  Observations  11401  11401  11184  11184  $$R^{2}$$  0.0616  0.0619  0.352  0.352  State FEs  Y  Y  Y  Y  Founding year FEs  Y  Y  Y  Y  Industry FEs  Y  Y  Y  Y  Industry $$\times$$ Founding Year FEs  Y  Y  Y  Y  Team size FEs  Y  Y  Y  Y     IPO/Acq.?  log exit value     (1)  (2)  (3)  (4)  Founder replaced?  –0.0472**     –0.211**        (0.0198)     (0.0881)     Founder-CXO replaced?     –0.0577***     –0.289***        (0.0170)     (0.0773)  Constant  0.302***  0.300***  –0.475  –0.486     (0.0551)  (0.0553)  (0.407)  (0.408)  Observations  11401  11401  11184  11184  $$R^{2}$$  0.0616  0.0619  0.352  0.352  State FEs  Y  Y  Y  Y  Founding year FEs  Y  Y  Y  Y  Industry FEs  Y  Y  Y  Y  Industry $$\times$$ Founding Year FEs  Y  Y  Y  Y  Team size FEs  Y  Y  Y  Y  The table reports ordinary least-squares (OLS) regressions of firm-level outcomes on indicators for whether the startup had one of two types of founder replacement. The unit of observation is a VC-backed startup. “Founder replaced?” is equal to one if at least one of the founding team members was observed replaced before the exit or end of the sample. “Founder-CXO replaced?” is one if one of those replaced had the CXO title (e.g., Chief Technology Officer [CTO], CFO, or CEO). The dependent variable in Columns (1) and (2) is a dummy equal to one if the firm had an IPO or acquisition with a valuation greater than 1.25 times the capital invested by the end of the sample period (April 2017). The last two columns report the log of exit valuation (if known, otherwise assumed to be 25% of invested capital). If unknown, exit value is assumed to be 25% of capital invested. Fixed effects include the headquarters state, founding year, industry, the interaction of industry and founding year and indicators for the size of the founding team. Unreported is a control for the log of first capital invested. Standard errors clustered at the founding year reported in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. We cannot draw causal conclusions from Table 6 for several reasons. Venture capitalists may be more likely to replace founders when their startups are struggling, and founders may be more likely to relinquish their roles when prospects appear bleak. We propose an instrumental variables approach below. 3. Instrumental Variables The replacement variable $$R_{i}$$ is likely correlated with the current and future prospects of the entrepreneurial firm, both omitted from (1). For example, replacement may coincide with unobserved negative shocks to the firm that would lower future performance or VC investors may seek to replace founders only in firms that have better prospects unconditionally. We require a variable $$Z$$ that predicts the likelihood of replacement but does not belong in Equation (1) (i.e., exclusion restriction). Our instrument proxies for changes to the supply of potential replacement executives from other companies using plausibly exogenous changes to the ease of their recruitment. As finding replacement executives is nontrivial, changes to the pool of available executives could affect the both rate of founder replacement and the quality of replacements recruited. Some of the most attractive replacement executives will be those with experience at the sort of company that might acquire the focal startup, especially for a private firm that may be struggling and for whom an acquisition might seem the most promising exit. Table A1 in the Online Appendix shows the most frequent prior employers of the incoming replacement executives in our sample are large, established firms. This is consistent with the “professionalization” notion that new, incoming replacements are not fresh entrepreneurial blood but rather seasoned executives from established firms. Given that these large firms are an attractive source of replacement executives, exogenous changes to inter-organizational mobility act as a shock to the supply of replacement executives for VC-backed firms.14 In an ideal experiment, the researcher would randomly restrict the ability for the firm or VC to replace a founder of their choice. For example, one could simply impose a no-firing rule or otherwise restrict labor mobility in the firm’s industry. Doing so eliminates any selection issues (e.g., the VC picks the companies that have the best prospects to replace, or those that need replacement are worse firms) and can isolate causal effects. Our proposed instrument exploits changes in labor laws that, in turn, may affect the supply of replacement executives. There are three possible outcomes. First, the cause of the firm’s struggles could be the “jockey” (i.e., current management) and not the “horse” as suggested by Kaplan, Sensoy, and Strömberg (2009) in their analysis of firms that eventually have an IPO. The VC may not have already replaced management, either because they want to be perceived as patient or because the management team is entrenched. Second, replacement might improve firm prospects because the existing match between the founder and the firm limits growth and exit opportunities. Third, replacement could have a negative impact on performance if founders are important assets and the VC incorrectly assesses their value. 3.1 Employee non-compete agreements and executive replacements One factor affecting the inter-organizational mobility of replacement executives is policy regarding post-employment covenants not to compete. Non-compete agreements are sections of employment contracts in which a worker covenants neither to join nor to found a rival firm within 1–2 years of leaving. A growing body of work shows that non-compete agreements bind employees to their employers, thus making it difficult for small companies to attract workers away from established firms (Stuart and Sorenson 2003). Garmaise (2011) shows that firms use non-compete agreements with at least 70% of their top executives, who are likely candidates to be targeted as replacements for founders (e.g., Table A1 in the Online Appendix). Marx, Strumsky, and Fleming (2009) provide causal evidence linking the enforceability of non-compete agreements to worker mobility, leveraging an unintentional 1985 reversal of non-compete policy in Michigan. These shocks to the supply of executives should—given fixed demand—alter the VC’s opportunity cost of either replacing or retaining the existing founding team. Importantly, non-compete agreements are more likely to be enforced against top or high-quality management that the established firm most wants to retain. Thus, the changes induced by the law will increase or decrease the supply of higher-quality replacement executives. The Michigan reversal occurred well in advance of our sampling period, but several changes in other states facilitate analysis using our data. Our methodology for finding changes in non-compete policy is as follows. We reviewed Malsberger, Brock, and Pedowitz (2016), the definitive reference regarding both legislative and judicial changes to state-by-state policy regarding non-compete agreements, and made a list of changes during the time period of our data set. We also searched Lexis/Nexis for state Supreme Court decisions possibly affecting non-compete agreements. Approximately three dozen legislative or judicial changes appeared potentially material. We then enlisted the expertise of two prominent employment lawyers to assess the impact of these, leaving 14 material shifts to enforceability during our time period. During our sample period, nine states strengthened the enforceability of employee non-compete agreements: Florida (1996), Ohio (2004), Vermont (2005), Idaho (2008), Wisconsin (2009), Georgia (2010), Colorado (2011), Illinois (2011), and Texas (2011). Importantly, we require that the law changes were not related to the future prospects of the startups in the state. For changes due to decisions not handed down by a state Supreme Court, which are plausibly exogenous, we provide background on the political economy of the change. Florida (1996): The change in Florida was pushed for (and codrafted by) the Florida Bar Association, as attorneys in the state had become frustrated with the lack of clarity regarding enforceability of employee non-compete agreements and found it difficult to advise their clients with certainty, and not for the purpose of affecting startup outcomes.15 Ohio (2004): In Lake Land v. Columber, the state Supreme Court resolved a dispute between various courts of appeals in the state regarding whether continued employment was sufficient consideration to uphold a non-compete. Following this decision, firms no longer had to offer particular consideration (e.g., compensation, training, or promotion) when asking an existing employee to sign a non-compete. Vermont (2005): Similar to Ohio’s 2004 verdict, the decision in Summits 7 v. Kelly resolved a division among local trial courts by stating that continuing employment is sufficient consideration for a so-called “afterthought” non-compete requested after an employee starts working. Idaho (2008): The Idaho law, which among other provisions enacted what is commonly called a “blue-pencil” rule whereby which a judge facing a lawsuit is allowed to modify the contract to make it more reasonable, was advocated by the Idaho Falls based Melaleuca health products company (Hopkins 2008). Wisconsin (2009): The State Supreme Court decision in Star Direct v. Dal Pra had a significant impact on enforceability by upholding “red pencil” reformation of contracts. Without reformation, judges would refuse to enforce unreasonable non-compete agreements. With red-pencil reformation, a judge can strike unacceptable parts of the contract but retain the rest. Such a capability may give firms incentives to write unreasonable contracts that yield an in terrorem “chilling effect” among employees but are nonetheless partially enforced in court. A 2015 decision further strengthened enforceability by confirming that continued at-will employment sufficed as consideration for a post-hire non-compete. Georgia (2010): Georgia added a blue-pencil provision, with its change brought about by a 2010 referendum which amended the state constitution.16 However, the text of the referendum has been criticized as misleading as it did not make direct reference to employee non-compete covenants, so the reversal can reasonably be characterized as unanticipated.17 Colorado (2011): The state Supreme Court ruling in Luncht’s Concrete Pumping v. Horner brought Colorado into the predominant practice that continued employment is sufficient consideration for a non-compete, as opposed to requiring additional compensation (or a promotion) in exchange for signing the non-compete after having already started at the firm. Illinois (2011): The state Supreme Court decision in Reliable Fire Equipment v. Arredondo fundamentally changed how enforceable non-compete agreements are in Illinois. Previously, the state had imposed stringent requirements for establishing a “legitimate business interest”, but Reliable Fire changed the old rigid test into a more flexible one, making it easier to enforce non-compete agreements. Texas (2011): The state Supreme Court decision in Marsh v. Cook aligned Texas non-compete law with other states with respect to consideration. Prior the decision, the consideration had to “give rise” to the interest being protected, which resulted in very little actually be protectable (primarily just trade secrets). Marsh changed that test: thereafter, consideration for a non-compete could be far more broad. Thus Texas became a state where it is not nearly as hard as it had been to have an enforceable non-compete. During the same period, five states weakened the enforceability of non-compete agreements: Louisiana (2001), Oregon (2008), South Carolina (2010), New Hampshire (2012), and Kentucky (2014).18 Louisiana (2001): The changes in Louisiana was enacted by the Supreme Court, which in Shreveport Bossier, Inc. v. Bond ruled that the state’s non-compete agreements could only restrict entrepreneurship and not simply moving to a rival firm. That the change was enacted by the SSC cannot be reasonably construed as anticipating future startup performance. (Note that this change was partially undone in 2003 by a new law.) Oregon (2008): Oregon’s Commissioner of Labor successfully lobbied to passed a bill that would invalidate non-compete agreements if workers were not told about the covenant until after they accepted their offer out of employment.19 South Carolina (2010): In Poynter Investments v. Century Builders of Piedmont, the state Supreme Court ruled against the use of “blue pencil” provisions whereby a court can reform (i.e., soften the terms of) an unenforceable non-compete instead of striking it down as invalid. At the same time, the Court made it easier for firms to obtain a preliminary injunction against ex-employees, so the impact of the SC ruling may be tempered. (Results are robust to treating SC as weakening enforceability, strengthening it, or not affecting it.) New Hampshire (2012): A similar measure was brought about in 2012 by a New Hampshire state representative who had personally been negatively affected by a non-compete,20 suggesting that this reform was undertaken not out of a desire to promote the performance of startups but rather as a workers’ rights measure. Kentucky (2014): In Creech v. Brown the state Supreme court ruled that continued employment was not sufficient consideration for a non-compete entered into after an employee started work at a new firm. In sum, the changes in non-compete enforceability appear not to have been motivated by the prospects of startups in those states. By contrast, Hawaii’s 2015 reform, which banned non-compete agreements in the IT industry, was explicitly taken up in order to foster entrepreneurial activity. Our instrumental variable captures these labor law changes across time and US states in our sample period. Defined in detail below, the variable identifies whether a startup active in a given state experienced a change in non-compete law—whether strengthening or weakening—or had no change in labor laws. For the set of startups in states that weakened non-compete laws, we expect such a change to make it relatively easier to replace founders. Alternatively, those states that strengthened their non-compete rules should exhibit relatively fewer replacements as the supply of possible replacement executives is smaller. 3.2 External validity Are these states in which non-compete laws changed representative of VC-backed firms during our sample period? The 14 states with non-compete reforms used in our analysis comprise 17.2% of overall VC investments. Given that 41.4% of all VC investments are in California, the treated states compose nearly 30% of the remaining startups in the United States. Moreover, 32.1% or nearly one-third of all venture capitalists have portfolio companies in the treated states. Table 7 compares more variables for startups in the treated states to those in all other states in our sample period. The third column reports the full sample means for each variable. The first observable differences show up in capital raised. Startups in treated states raise nearly a million dollars more in their initial round but $5MM less during their lifetime, although startups in both types of states have a similar number of rounds. Startups in treated states have lower rates of IPOs and acquisitions though similar failure rates as untreated states. This difference means that the treated firms in the IV regression start with a lower chance of success as measured by the dependent variable. Rates of founder replacement are roughly equivalent between treated and untreated states. Table 7 Comparison of VC activity in IV versus non-IV states    Never treated  Treated state  Total  Year firm founded  2001.1  2000.7  2001.0  Year first VC  2002.5  2002.5  2002.5  First capital raised  6.303  7.285  6.472  Total equity financings (all)  3.538  3.478  3.528  Total capital raised (m)  38.42  33.43  37.56  Information technology  0.539  0.523  0.536  Biotech  0.185  0.174  0.183  Went public  0.0637  0.0438  0.0603  Acquired  0.414  0.409  0.413  Still private  0.242  0.245  0.242  Out of business  0.280  0.301  0.284  Founder replaced?  0.153  0.146  0.152  Portfolio size of VC investor  82.91  63.57  79.58  Firm raised from top 10% VC  0.699  0.590  0.680     Never treated  Treated state  Total  Year firm founded  2001.1  2000.7  2001.0  Year first VC  2002.5  2002.5  2002.5  First capital raised  6.303  7.285  6.472  Total equity financings (all)  3.538  3.478  3.528  Total capital raised (m)  38.42  33.43  37.56  Information technology  0.539  0.523  0.536  Biotech  0.185  0.174  0.183  Went public  0.0637  0.0438  0.0603  Acquired  0.414  0.409  0.413  Still private  0.242  0.245  0.242  Out of business  0.280  0.301  0.284  Founder replaced?  0.153  0.146  0.152  Portfolio size of VC investor  82.91  63.57  79.58  Firm raised from top 10% VC  0.699  0.590  0.680  The table reports startup and investor observables for two samples. The first column (“Never treated”) reports means of each variable for the states that did not have a non-compete law change in our sample period. The second column (“Treated state”) reports the same means for the states with such law changes. The last column (“Total”) reports the full sample means. “Portfolio size of VC investor” is the count of number of unique entrepreneurial firm investments made by the startup’s investors as of the firm’s exit. The variable serves as a proxy for experience. The variable “Firm raised from top 10% VC” is one if at least one of the entrepreneurial firm’s investors was in the top 10% of this portfolio size variable. Table 1 defines the other variables. A key feature of the data construction for the IV analysis described below is the use of portfolio firms belonging to VCs who invested in startups treated by the changes in non-compete law. The variable “Portfolio size of VC investor” shows that VCs investing in treated states have 19% smaller portfolios. The variable “Firm raised from top 10% VC” is one if at least one of a startup’s investors is in the top 10% of investing experience by the end of the sample. Treated-state startups are nearly 11% less likely to have such an investor. This difference is as expected, but we believe reasonably close. Overall, there do not appear to be large economic differences in observables between firms and investors in the treated states. Thus we believe the IV results generalize to the average VC-backed firm in our sample period. 3.3 Is there home bias in hiring? We take as our treatment group startup companies active and VC-backed in these 14 states at the time these legal changes took effect. For the non-compete reversals above to have affected the ability of startup companies in those states to recruit replacement executives, there must be a material “home bias” in recruitment. In other words, although startups could (and do) recruit replacement executives from other states, the non-compete reversal should have an effect only if the startups disproportionately recruit replacement executives from the same state where they are located. To establish home bias, it is not sufficient to merely count the proportion of replacement executives that come from the same state, as states have different supplies of potential replacements. We proceeded to build a baseline of the percentage of public firms in each state in order to inform the likelihood that a replacement executive would come from the same state as the focal startup. We did this for the IT and Health care sectors, for which we could match directly the classification codes from VentureSource to Compustat. IT and Health care represent 68% of all VC-backed ventures in our full sample. The next step was to compare the same-state replacement rate for IT and Health care startups in each state to the percentage of public companies in those states to determine whether there is a “home bias.” This required looking up the location of the replacement executives. A research assistant was tasked with finding the prior work location—not simply the company headquarters—of all 1,991 replacement executives. Sources included LinkedIn, ZoomInfo, BusinessWeek, and others. Reliable data was available for 1,373 replacement executives; the remainder were either not locatable or could not be disambiguated between multiple locations. For the replacement executives for whom we could not reliably establish their previous geographical location, the firms that hired them did not differ significantly in terms of year of founding, the amount of capital raised in the first round, or the total rounds of funding. We find substantial “home bias” in the recruitment of replacement executives. First of all, every state with at least ten replacements (and all but one state with five or more replacements) has evidence of a home bias. Even in California, which as mentioned above is home to 26% of public IT and Health care companies, there is a home bias of more than double as 65% of replacement executives are recruited from within the state. Moreover, we note that each of the states with a non-compete reversal used for our instrument exhibits a home bias from 8.6 to 15 times.21 Of course, the above does not control for possibly confounding factors, so we next turn to multivariate analysis. Table 8 analyzes several sources of bias in the selection of replacement executives. For each replacement, we have 50 observations corresponding to U.S. states. The dependent variable is set to one if the replacement for that focal firm’s departing founder came from that state. Column (1) formally tests our home bias hypothesis. The estimate of the coefficient on the startup being in the focal state is positive and statistically significant in all models. The marginal effect on the probability of the replacement coming from that same state is 7.9%. In Column (2), we add additional VC-related controls, including whether the VC is in the same state as the replacement and the (logged) count of the VCs investments in that state. Although both of these are estimated with positive and statistically significant coefficients, their marginal effects are an order of magnitude smaller than home bias. Table 8 Geographic bias in recruitment of replacements for founders    Replacement executive from state?     (1)  (2)  (3)  (4)  Startup in focal state?  2.436***  1.689***  1.630***  1.578***     (0.0439)  (0.0547)  (0.0624)  (0.0640)  Any of startup’s VCs in focal state?     0.572***  0.365***  0.288***        (0.0419)  (0.0502)  (0.0511)  Log first capital raised     0.0616***  0.0303**  0.0220*        (0.0126)  (0.0122)  (0.0118)  Total financings     –0.0151***  –0.00697*  –0.00340        (0.00428)  (0.00419)  (0.00400)  log total capital raised     –0.0722***  –0.0627***  –0.0520***        (0.0124)  (0.0118)  (0.0111)  log # investments of startup’s     0.147***  0.0545***  0.0190***  $$\quad$$ VCs in focal state     (0.00648)  (0.00625)  (0.00593)  log # public firms in industry        0.271***  –0.514***  $$\quad$$ in focal state        (0.0184)  (0.122)  Constant  –2.357***  –2.707***  –3.844***  –4.010***     (0.0533)  (0.0929)  (0.127)  (0.404)  Observations  74850  73300  57850  43966  Pseudo-$$R^{2}$$  0.338  0.405  0.442  0.432  Number startups  1373  1345  1054  1054  Industries  All  All  IT, Health care  IT, Health care  Founding year FEs  Y  Y  Y  Y  Year 1st fin. FEs  Y  Y  Y  Y  Industry FEs  Y  Y  Y  Y  Replacement state FEs  N  N  N  Y     Replacement executive from state?     (1)  (2)  (3)  (4)  Startup in focal state?  2.436***  1.689***  1.630***  1.578***     (0.0439)  (0.0547)  (0.0624)  (0.0640)  Any of startup’s VCs in focal state?     0.572***  0.365***  0.288***        (0.0419)  (0.0502)  (0.0511)  Log first capital raised     0.0616***  0.0303**  0.0220*        (0.0126)  (0.0122)  (0.0118)  Total financings     –0.0151***  –0.00697*  –0.00340        (0.00428)  (0.00419)  (0.00400)  log total capital raised     –0.0722***  –0.0627***  –0.0520***        (0.0124)  (0.0118)  (0.0111)  log # investments of startup’s     0.147***  0.0545***  0.0190***  $$\quad$$ VCs in focal state     (0.00648)  (0.00625)  (0.00593)  log # public firms in industry        0.271***  –0.514***  $$\quad$$ in focal state        (0.0184)  (0.122)  Constant  –2.357***  –2.707***  –3.844***  –4.010***     (0.0533)  (0.0929)  (0.127)  (0.404)  Observations  74850  73300  57850  43966  Pseudo-$$R^{2}$$  0.338  0.405  0.442  0.432  Number startups  1373  1345  1054  1054  Industries  All  All  IT, Health care  IT, Health care  Founding year FEs  Y  Y  Y  Y  Year 1st fin. FEs  Y  Y  Y  Y  Industry FEs  Y  Y  Y  Y  Replacement state FEs  N  N  N  Y  The table analyzes possible sources of geographic bias in the recruitment of replacements for 1,999 founders. Each observation is a replacement-state dyad, 50 observations per founder replacement. The dependent variable is 1 if the incoming replacement for the founder at a given startup was recruited from that state. “Startup in focal state?” captures whether the startup is headquartered in the focal state (i.e., the state for that replacement-state dyad). “Any of startup’s VCs in focal state?” captures whether some VC that invested in the focal startup is headquartered in the focal state. “Log # investments of startup’s VCs in focal state” reports the number of investments in the focal state made by all of the VCs who invested in the focal startup. Columns (1) and (2) are estimated on the full sample of founder replacements. The sample in Columns (3) and (4) is estimated on founder replacements at IT and Health care startups because direct matches to Compustat counts of public firms are available only for those two categories. “Log # public firms in industry in focal state” is the number of firms in either IT or Health care that were in the focal state (for IT or Health care startups, respectively). Table 1 defines the other variables. Robust standard errors are reported in parentheses, clustered at the state level. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. Column (3) introduces a control for the number of public firms in the same state as the replacement. Doing so requires mapping industry categories from VentureSource to Compustat. The only two categories that map directly are Information Technology and Health care, so the remainder of the table is restricted to these industries. Like in the previous column, although there is a positive association between the likelihood of replacement and the presence of public firms from the same industry (at least for IT and Health care), the estimated coefficient is again an order of magnitude smaller than for home bias. Column (4) adds state fixed effects, with consistent results. 3.4 IV sample construction Within the treated states, we consider two sets of startups. First, we construct a sample of startups affected by the change in labor laws. Startups must receive their first round of capital before the law change, still be active (nonexited) by this date and have had no founder replacements. These startups are at risk of replacement and are affected by the change in the labor supply from the enforceability change. Note that we do not select firms based on any post-law-change behavior (including follow-on investments) as such could introduce confounds from selection into treatment. Similarly, including startups founded or first financed after the law change introduces both selection (i.e., different firms are founded because of the new law) and the treatment effects of interest. The next challenge in satisfying the exclusion restriction is the comparison or control sample. We cannot simply track the same entrepreneurial firm over time because once a founder is replaced in a single-founder firm (a large fraction of the sample), the firm can no longer receive treatment. Rather, we require some set of firms that were not affected by the law yet were at risk of having their founders replaced. Such firms would ideally face similar economic and legal settings as those startups affected by the law change. That is, we would like to compare these treated startups to ones based in the same state, financed at the same time and in the same industry but for some random reason are not affected by the labor law change. Such a sample is not available, but we present an alternative that exploits both within and across-state variation. One approach would be to include all startups not affected by the law changes, but doing so would likely introduce a large set of unobservably dissimilar firms, particularly with regard to unobserved trends. Such trends might capture changes in startup success instead of the proposed treatment effect. Our approach exploits knowledge about the treated startups’ investors and their portfolios. Constructing the control group proceeds by identifying all VC investors of the treated startups defined above. Rather than include all VC-backed firms financed during the same years, we narrow the sample to those in the portfolios of these VC investors who invested in treated startups and who were headquartered in one of the treated states. Such a restriction excludes VCs who for example only invested in California or only in Washington (both states had no law change). How does the restriction of VC portfolios with some treatment exposure help address identification issues? The tendency of VCs to invest in similar-quality startups within an industry helps to ensure that the treated and control startups exhibit similar unobserved trends. VCs in our sample also typically invest out of a fund or two, of which each selects startups of similar development stage and industry. Controlling for firm founding year, firm state headquarters, financing stage, total capital raised and round number addresses cross-sectional differences in firm maturity that could affect replacement rates. Estimation of Equation (3) using this sample mimics estimators that exploit staggered law changes. The main difference here is that we do not include startups financed after the law changes because the law change likely affected both the types of startups financed and their ability to replace managers. We thus need to focus on a sample of startups who were founded and financed before the law changes but that have differential exposure to the changes. Startups in treated states act as controls for within-state startups and other startups financed at the same time. The inclusion of state fixed effects allows us to control for time-invariant differences across the treated states, while implying that identification of the effect of replacement comes from within-state variation before the law change year. Inclusion of startups outside of treated states in a model that also includes state fixed effects would not provide any identification for the instrumental variable and are thus excluded. Table 9, Column (1) presents the results of the Equation (1) estimated using the sample of startups in treated states. This table shows a negative and statistically significant association between replacing founders and eventually achieving an attractive liquidity event, consistent with Table 6 above. Thus it does not appear that the IV sample is materially different from the overall sample in this respect. As discussed above, this correlation could be downward biased given that investors are more likely to dismiss founders in struggling companies (or that founders are also more likely to resign voluntarily, necessitating their replacement). Table 9 Founder replacement and firm outcomes: Instrumental variables    IPO/Acq.?  Replaced?  IPO/Acq.?  log exit value     OLS  First stage  2SLS  OLS  2SLS     (1)  (2)  (3)  (4)  (5)  Founder replaced  –0.0451*     0.232**  –0.202  1.399**     (0.0236)     (0.112)  (0.132)  (0.592)  Increased Enforceability     –0.758***                 (0.127)           Log capital stock  0.0307**  0.306***  0.0146*  1.129***  1.037***     (0.0111)  (0.0373)  (0.00839)  (0.0354)  (0.0496)  Syndicate size  0.00148  0.0529  –0.00361  0.0530  0.0272     (0.0129)  (0.0860)  (0.0173)  (0.0787)  (0.0821)  Profitable at financing  –0.00154  –0.190*  0.0130  0.0508  0.133     (0.0212)  (0.104)  (0.0235)  (0.100)  (0.108)  Constant  0.203**  –1.779***  –0.121*  –1.320*  –2.700***     (0.0853)  (0.499)  (0.0725)  (0.709)  (0.449)  Observations  1341  1341  1341  1326  1326  $$R^2$$  0.0472  0.191  .  0.516  .  1st stage F-stat     35.42           Financing year FEs?  Y  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Y  Round # FEs?  Y  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  Y     IPO/Acq.?  Replaced?  IPO/Acq.?  log exit value     OLS  First stage  2SLS  OLS  2SLS     (1)  (2)  (3)  (4)  (5)  Founder replaced  –0.0451*     0.232**  –0.202  1.399**     (0.0236)     (0.112)  (0.132)  (0.592)  Increased Enforceability     –0.758***                 (0.127)           Log capital stock  0.0307**  0.306***  0.0146*  1.129***  1.037***     (0.0111)  (0.0373)  (0.00839)  (0.0354)  (0.0496)  Syndicate size  0.00148  0.0529  –0.00361  0.0530  0.0272     (0.0129)  (0.0860)  (0.0173)  (0.0787)  (0.0821)  Profitable at financing  –0.00154  –0.190*  0.0130  0.0508  0.133     (0.0212)  (0.104)  (0.0235)  (0.100)  (0.108)  Constant  0.203**  –1.779***  –0.121*  –1.320*  –2.700***     (0.0853)  (0.499)  (0.0725)  (0.709)  (0.449)  Observations  1341  1341  1341  1326  1326  $$R^2$$  0.0472  0.191  .  0.516  .  1st stage F-stat     35.42           Financing year FEs?  Y  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Y  Round # FEs?  Y  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  Y  The table reports OLS and 2SLS estimates for founder replacement and startup outcomes in the 14 states that experienced changes in the enforceability of employee non-compete agreements. The unit of observation is a startup headquartered in one of these states and first financed before the non-compete changes. The sample of startups is described in Section 3. Column (1) regresses a dummy variable for whether a startup has an IPO or attractive acquisition on a set of controls. The control “Founder replaced” is one if a startup had at least one founder replaced on the executive team. “Increased Enforceability” corresponds to whether the state in which a focal startup is headquartered changed its non-compete laws; values of 1, and $$-1$$ represent an increase in enforceability and a decrease in enforceability, respectively. Other controls are as defined in Tables 1. Column (2) reports the first stage probit estimates where the replacement dummy is instrumented by “Increased Enforceability” given the policy change in that startup’s state. “1st. stage F” is the Cragg-Donald Wald F weak instruments statistic. Column (3) reports the two-stage least squares second-stage estimates. Columns (4) and (5) have instead as the dependent variable the log of the exit valuation (set to 25% of capital raised if the firm failed, had an unknown exit valuation or was still private by the end of the sample). “Financing year FEs” are fixed effects for the financing year prior to the reference law change year and “Round # FEs” are fixed effects for the financing round number. “Industry FEs” are fixed effects for the seven major industries in VentureSource. “Founding year FEs” are fixed effects for the startup’s founding year. “State FEs” are fixed effects for the startup’s headquarter state. Robust standard errors are reported in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. 3.5 Empirical model If changes in the enforceability of non-compete agreements affect the supply of available executives, then they should predict differential founder replacement after the law change for treated firms compared to control firms. Let the variable $$I_{i}$$ represent if and how non-compete enforceability changed for a startup active in a treated state, taking on values ${$-$ 1, 0, 1}$ which correspond to loosening of enforceability, no change, and tightening enforceability (similar to the variable in Garmaise 2011). Startups that either exited or had a founder replacement before their state’s non-compete change will have $$I_{i}$$ set to zero. Thus, this variable can be separately identified from the state fixed effects. The reduced form first stage regression that relates replacement to changes in non-compete laws is then:   \begin{equation} \text{R}_{i} = \rho_0 + \rho_1 X_{i} + \rho_2 I_{i} + \gamma_t +\phi_{\it State(i)} + \epsilon_{i}. \end{equation} (2) Again, $$R_{i}$$ is whether a founder was replaced after the focal policy reversal. $$X_{i}$$ are firm $$i$$ controls such as capital raised, syndicate size, and profitability. The $$X_i$$ also include round and industry fixed effects, while $$\gamma_t$$ is the financing year fixed effect and $$\phi_{\it State(i)}$$ is the state fixed effect. The estimate of $$\rho_2$$ reveals whether there is a reduced form correlation between changes in non-compete enforceability and founder replacement ($$R_{i}$$). We predict that increased enforceability should lead to relatively fewer replacements ($$\rho_2 < 0$$). The second stage is now:   \begin{equation} \textrm{Y}_{i} = \delta_0 + \delta_1 R_{i} + \delta_2 X_{i} + \gamma_t + \phi_{\it State(i)} + u_{i}. \end{equation} (3) where $$R_i$$ is instrumented from Equation (2). The dependent variable $$Y_i$$ includes the exit outcomes studied in Table 6: whether the startup achieves a quality exit, and also the log exit value. Table 9 contains the results of our instrumental variable regression, first for the liquidity outcome and then for the log value of the exit. Column (2) presents the first stage estimates of (2) used in the two stage least squares.22 The estimate of the coefficient on “Increased Enforceability” (i.e., $$\rho_2$$) is economically and statistically significant, with the predicted negative sign. The weak instruments F-statistic (e.g., Stock and Yogo 2005) exceeds the conventional required level. The results suggest that founder replacement is indeed sensitive to the supply of available executives in the same state who might take the founder’s executive role. The sign on the IV is also as expected: increased enforceability correlates with a lower probability of replacement. The second-stage estimate in Column (3) presents the instrumented coefficient for replacements $$R_{i}$$.23 Two results emerge. First, the coefficient is positive and significant, suggesting a positive treatment effect. Second, the sign of the coefficient on founder replacement reverses between the naive regression in Column (1) and also in Table 6, where it is negative, and the 2SLS result in Column (3), where it is positive. The economic magnitude of the estimate can be determined by the predicted probability of replacement from the first stage in column (2). A one-standard-deviation shift in this probability of predicted replacement (14%) implies a 25% increase in the probability of a liquidity event relative to the mean. The reversal of coefficient signs between the naive OLS and 2SLS imply a downward bias, which likely stems from a selection of relatively worse firms requiring VC intervention through founder replacement.24 The estimates suggest a positive causal effect of founder executive replacement in VC-backed firms. In the remaining columns of Table 9 we examine an alternative dependent variable: log of the exit value. Here, the naive cross-sectional analysis in Column (4) would indicate that founder replacement correlates with worse exit valuations. These patterns reassuringly resemble those of Table 6. Again, the second-stage estimates in Column (5)—the first stage is identical to Column (2)—show a positive correlation between replacement and exit values. 4. Decomposing the Positive Impact of Replacement on Venture Outcomes The results in Table 9 demonstrate a positive causal effect of founder replacement of firm exit outcomes. In this section, we attempt to disentangle how this value is created. Although we saw above a correlation between investor power and replacement (Table 5), we cannot state categorically that all replacements are involuntary. Rather, it may be that some founders relinquish their roles voluntarily but stay on, contributing in a different capacity. The combined human capital of an original founder and “new blood” may represent a net positive for the firm, suggesting that the benefit is more of an augmentation story about bringing in new executives to increase the pool of skills, and with founders making accommodations for those new executives by taking on a new formal role (even if their day-to-day responsibilities change little). Such a story would stand in contrast to the “professionalization” story of Hellmann and Puri (2002). Alternative explanations might also include that the incoming executives act in large part as “coaches” for the original founders, grooming them on a temporary basis so that they can later re-assume their former responsibilities. To assess the mechanisms at play, we decompose our instrumental-variables analysis along two axes: the replaced founder’s role and whether the replaced founder stays with the firm. We first exploit variation in the types of founders replaced, by using their titles prior to replacement. As is visible in Table 5, those who hold a CXO role are considerably more likely to be replaced than others. It is plausible that replacing top executives who have more decision-making power at the firm should have bigger benefits to the firm than replacing lower-level executives. Columns (1) and (2) of Table 10 consider two alternative indicators for replacement that split the main variable from Table 9: founders with CXO titles and those with titles below this rank (i.e., VP level).25, The positive causal effect of replacement is stronger in Column (1). Note that we cannot reject the null that coefficients across Columns (1) and (2) are different due to the naturally large standard errors in IV. In fact, they capture different types of replacement. Table 10 Differences in the effects of replacement    Founder type  Separating versus Accommodating     (1)  (2)  (3)  (4)  Founder-CXO replaced  0.326**              (0.163)           Non-CXO founder replaced     0.543              (0.488)        Founder replaced and left        0.290*              (0.164)     Founder replaced and stayed           0.714              (0.533)  Constant  –0.115  –0.101  –0.113  –0.0886     (0.101)  (0.0760)  (0.102)  (0.0784)  Observations  1287  1120  1210  1120  Controls?  Y  Y  Y  Y  Financing years FE?  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Round # FE?  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y     Founder type  Separating versus Accommodating     (1)  (2)  (3)  (4)  Founder-CXO replaced  0.326**              (0.163)           Non-CXO founder replaced     0.543              (0.488)        Founder replaced and left        0.290*              (0.164)     Founder replaced and stayed           0.714              (0.533)  Constant  –0.115  –0.101  –0.113  –0.0886     (0.101)  (0.0760)  (0.102)  (0.0784)  Observations  1287  1120  1210  1120  Controls?  Y  Y  Y  Y  Financing years FE?  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Round # FE?  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  The table reports additional specifications of the instrumental variables model in Table 9. The main replacement variable “Founder-CXO replaced” variable in Column (1) is a dummy if a replacement occurs and the replaced founder had a title of CXO (e.g., CFO or CEO). Column (2) includes an indicator for whether there was a replacement and the replaced founder had a title below CXO (i.e., VP). Columns (3) and (4) similarly compare replacements, here distinguished by whether the replaced founder leaves or stays after being replaced (i.e., “separating” vs. “accommodating”). The main variable in Column (3) is set to one only for founders who were replaced and left the firm, while the independent variable in Column (4) corresponds to founders who were replaced yet stayed at the firm. “Controls?” indicates the inclusion of all the controls reported and defined in Table 9. Robust standard errors are in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. Next, we compared the effect of replacements where the founder stays at the startup (i.e., “accommodating” replacements; Hellmann and Puri 2002) as opposed to leaving (“separating” replacements). As mentioned, above we collected career histories for 1,322 of the 1,999 replaced founders. These data allow us to conclude whether a replaced founder stayed with the company or, if not, how long after the replacement they departed. As noted above, it could be that that “accommodating” replacements are be more beneficial as the replaced founder’s human capital is not lost; rather, the firm’s total expertise is augmented by the arrival of the replacement executive. Moreover, an accommodating replacement may reflect less dissatisfaction with the founder’s performance than if s/he was forced out of the company (although we cannot cleanly distinguish involuntary from voluntary separation in our data). By contrast, following “separating” replacements bitterness may arise among founders if they were forced out, leading them to hire away key employees (who have allegiance to the deposed founder) at a new or existing rival. However, the estimates in Columns (3) and (4) of Table 10 suggest that the positive impact of founder replacement on startup performance is more evident among founders who leave the firm.26 This may be because a departed founder cannot cause conflict or undermine a replacement as is possible if the founder remains at the firm in a possibly-undesirable role. Although our data does not allow us to cleanly adjudicate between voluntary and involuntary replacement, this result may indicate that founders who are replaced yet accommodated with a different role can be disruptive to the forward progress of the startup. It also reinforces the notion that founder replacement is a key aspect of “professionalization” led by venture capitalist investors. 5. Robustness and Identification Assumptions 5.1 Nature of non-compete changes The instrumental variable regression exploits the staggered changes in 14 states, some of which were enacted by state Supreme Court decisions and others via the legislature. Each of these has strengths and weaknesses in terms of affecting policy. Court decisions are attractive because they are generally unpredictable and apply both to future and existing contracts (Jeffers 2017), but they may also be specific to the facts of the case and not apply broadly. Laws, by contrast, are more general in nature but are often written so as to address only future contracts entered into; the enforceability of previously executed non-compete agreements may not be affected if the new law is purely forward-looking. For example, when New Hampshire began requiring in 2012 that employees be given prior notice that they will be required to sign a non-compete, this law did not immediately invalidate all prior non-compete agreements in which the worker had not been given notice. The forward-looking nature of many laws is less of a problem when the aim of the law is to strengthen the enforceability of non-compete agreements. Firms can simply require their employees to sign updated employment contracts, at least where continued employment suffices as consideration, as the effective date will fall under the auspices of the new law.27 Indeed, following the passage of the 2010 Georgia non-compete law, Atlanta-based employment attorney Benjamin Fink of Berman Fink Van Horn recalled, “[Law f]irms definitely issued alerts when the new law went into effect and many employers revised their employment and restrictive covenant agreements to take advantage of the law” (Fink 2017). Doing so would only be rational, especially given that in most states, including Georgia, the only consideration required for an existing employee to sign a new non-compete is to remain in their existing job. By contrast, in states in which the law weakened the enforceability of non-compete agreements, firms would want to avoid updating their employment agreements so that existing employees would still be bound under the previous provisions. Thus in New Hampshire and Oregon, chances are that only newly hired employees would be affected by the weakened law, which may not have as strong of an effect as if enforceability were strengthened by a new law, or if the court had issued a ruling. Accordingly, in the first three columns of Table 11, we repeat the main IV regressions for the likelihood of a positive exit while omitting these two states. Results are similar. Table 11 Robustness tests    Omit law-based weakening  Omit Texas  Omit Colorado  Omit Illinois  Omit Georgia     OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS     (1)  (2)  (3)  (4)  (5)  (6)  (7)  (8)  (9)  (10)  (11)  (12)  (13)  (14)  (15)  Founder replaced  –0.0350     0.282***  –0.0198     0.227*  –0.0282     0.301***  –0.0393     0.244**  –0.0376     0.222**     (0.0301)     (0.103)  (0.0478)     (0.138)  (0.0341)     (0.113)  (0.0345)     (0.107)  (0.0304)     (0.112)  Increased enforceability     –1.265***        –0.933***        –1.267***        –1.331***        –1.348***           (0.204)        (0.217)        (0.231)        (0.224)        (0.212)     Constant  0.0447  –1.287**  –0.125*  0.238  –1.932***  –0.164*  0.300  –1.412**  –0.0792  0.260**  –0.940*  –0.182**  0.0898  –1.066*  –0.102     (0.109)  (0.520)  (0.0738)  (0.188)  (0.646)  (0.0909)  (0.174)  (0.587)  (0.0790)  (0.101)  (0.554)  (0.0775)  (0.152)  (0.562)  (0.0759)  Observations  1217  1217  1217  698  698  698  975  975  975  1022  1022  1022  1006  1006  1006  $$R^2$$  0.0453  0.207  .  0.0592  0.257  .  0.0358  0.206  .  0.0511  0.213  .  0.0336  0.225  .  1st stage F-stat     38.52        18.58        29.99        35.26        40.31     Controls?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Financing year FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Round # FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y     Omit law-based weakening  Omit Texas  Omit Colorado  Omit Illinois  Omit Georgia     OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS  OLS  1st stage  2SLS     (1)  (2)  (3)  (4)  (5)  (6)  (7)  (8)  (9)  (10)  (11)  (12)  (13)  (14)  (15)  Founder replaced  –0.0350     0.282***  –0.0198     0.227*  –0.0282     0.301***  –0.0393     0.244**  –0.0376     0.222**     (0.0301)     (0.103)  (0.0478)     (0.138)  (0.0341)     (0.113)  (0.0345)     (0.107)  (0.0304)     (0.112)  Increased enforceability     –1.265***        –0.933***        –1.267***        –1.331***        –1.348***           (0.204)        (0.217)        (0.231)        (0.224)        (0.212)     Constant  0.0447  –1.287**  –0.125*  0.238  –1.932***  –0.164*  0.300  –1.412**  –0.0792  0.260**  –0.940*  –0.182**  0.0898  –1.066*  –0.102     (0.109)  (0.520)  (0.0738)  (0.188)  (0.646)  (0.0909)  (0.174)  (0.587)  (0.0790)  (0.101)  (0.554)  (0.0775)  (0.152)  (0.562)  (0.0759)  Observations  1217  1217  1217  698  698  698  975  975  975  1022  1022  1022  1006  1006  1006  $$R^2$$  0.0453  0.207  .  0.0592  0.257  .  0.0358  0.206  .  0.0511  0.213  .  0.0336  0.225  .  1st stage F-stat     38.52        18.58        29.99        35.26        40.31     Controls?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Financing year FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Founding year FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Round # FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Industry FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  State FEs?  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  Y  The table reports OLS and 2SLS estimates for founder replacement and entrepreneurial firm outcomes. The unit of observation is a startup headquartered in one of these states and first financed before the non-compete changes. The sample of entrepreneurial firms is described in Section 3. Triads of columns inclue the OLS, first-stage, and 2SLS estimates. Columns (1)–(3) omit states in which the legislature enacted a law that weakened the enforceability of non-compete agreements, which may have less effect than other changes as described in section 3.1. Columns (4)–(15) conduct a series of “leave one out” tests by omitting each of the largest states in our sample: Texas, Colorado, Illinois, and Georgia. “Founder replaced” is one if a financing had at least one founder replaced on the executive team. Controls and fixed effects are as defined in Tables 9. Robust standard errors are reported in parentheses. Significance: * $$p<.10$$, ** $$p<.05$$, *** $$p<.01$$. 5.2 Single-state dependence Another question is whether the results depend entirely on the inclusion on any one of those states in particular. The remaining columns of Table 11 exclude in turn each of the largest treated states: Texas, Colorado, Illinois, and Georgia.28 These leave-one-out estimates are quantitatively and qualitatively similar. Thus it does not appear that one state is driving the main results. The results in the instrumental variables analysis are also robust to alternative definitions. Modifying the exit outcome dependent variable window from five years to two, three or four has no major impact on results (not reported, but available from the authors). The relationship between replacement and exit rates is stronger for shorter windows to exit. 5.3 Temporal separation of treated and control startups Another potential concern is that the inclusion of firms that exited or had a founder replaced many years before the law change in treated states might bias the estimates because there exist no contemporaneous treated startups. In particular, one might worry about the introduction of control firms that operated many years before the treated firms. In a series of unreported analyses, we limit the temporal distance from treated startups for this group of control startups. Specifically, for each VC that has a treated firm, we censor the control firms to 5 - 10 years before the earliest treated firm. Results (available from the authors) are robust. Thus we believe that the results are not driven by the inclusion of very early startups. 5.4 Exclusion restriction One might be concerned that shifts in the enforceability of non-compete agreements might affect venture outcomes. The literature on non-compete agreements does not address this possibility empirically, instead focusing on how such contracts affect the founding of new firms and their early growth (see Stuart and Sorenson 2003; Samila and Sorenson 2011; Starr, Balasubramanian, and Sakakibara 2015). Still, it is possible that non-compete agreements might affect venture outcomes either by affecting the market for talent, as described above, or for startups themselves (i.e., the acquisition market). To the latter point, Younge, Tong, and Fleming (2015) show evidence that enforceable non-compete agreements fuel the acquisition market for startups—presumably because it is easier to retain employees post-acquisition. If true, this would work against our finding. To the former point, the effect of non-compete agreements on hiring by startups is ambiguous. If non-compete agreements are unenforceable then startups can more easily hire workers away from established companies. But by the same token, it is easier for established companies to poach talent from startups if they cannot use non-compete agreements. Absent such evidence, we investigated the relationship between labor market fluidity and the success of venture-backed startup companies. We first check whether changes in non-compete enforceability correlate with overall performance of VC-backed firms, not just those in our IV sample. In Table A3 (see the Online Appendix), we regress state-level liquidity outcomes for venture-backed startups on the law change variable in our specification. Negative binomial analysis of the counts of IPOs and acquisitions given the number of active startups in the previous year, we find that performance correlates negatively with non-compete enforceability, but the coefficients are statistically insignificant and the implied marginal effects are small. Next, we check whether non-compete agreements facilitate venture outcomes by enabling hiring growth (again, the effect is theoretically ambiguous29). We investigate this question by merging the National Establishment Time-Series (NETS) data set, which contains employment data from Dun & Bradstreet, to firms in the sample (match rate of 62%). Table A4 in the Online Appendix resembles that of our above IV except that the endogenous variable is not founder replacement but rather a variable equal to one if the startup saw an increase in overall employment in the current year. We see the expected positive correlation between increased employment and startup success in a naive regression, but the first-stage using increase/decrease in the enforceability of non-compete agreements goes in the wrong direction and the $$F$$-statistic is small. Although the sign becomes negative in the second stage, this coefficient is very imprecisely estimated. The weakness of this result is compatible with our claim that the effect of non-compete agreements on venture outcomes is primarily through executive-level replacement as opposed to hiring more broadly. Although we cannot prove the exclusion restriction, we would have expected Table A4 to present very different results if the alternative labor-market fluidity channel were responsible for our claimed results. 6. Discussion and Conclusion This paper draws a causal link between founder replacement and startup performance. Using data on VC-backed startups in the U.S. founded from 1995 to 2008, we show that although it may appear that replacing founders hurts startup performance, this is due to selection. We introduce exogenous variation in the ability of investors to find qualified replacements by exploiting changes in the enforceability of employee non-compete agreements in 14 states. Non-compete agreements make it more difficult to hire talent, especially among the sort of established-company executives who would be attractive replacements for founders. Instrumenting our regressions reverses the result of the naive regression, indicating that founder replacement boosts the performance of startups. We find moreover that the most consequential replacements are of founders who hold CXO-level titles. Further, the positive impact of replacement appears to be stronger in “separating” replacements, that is, when founders subsequently leave the company. Taken together, these results paint a picture of activist investors “professionalizing” the nascent firm. We most directly build on four papers that explore founder replacement, three using detailed survey data from samples of 50–200 firms (Hellmann and Puri 2002; Wasserman 2003; Kaplan, Sensoy, and Strömberg 2009) and one using register data from Denmark (Chen and Thompson 2015). Our results particularly echo Hellmann and Puri’s (2002) notion that VCs “professionalize” their portfolio companies, adding a causal link. Our results complement those of Bernstein, Giroud, and Townsend (2016) and Chemmanur, Krishnan, and Nancy (2011), who have sought causal evidence regarding whether investors provide “more than money” by monitoring the progress of their portfolio firms. Although Gorman and Sahlman (1986) reveal areas in which investors spend time, we do not know which of these activities create real value. This study shows that the replacement of executives by investors is a key mechanism by which investors improve the performance of their portfolio companies. More generally, we contribute to a perennial debate in the venture capital literature regarding the value of the VC firm and partner (Ewens and Rhodes-Kropf 2015; Hellmann and Puri 2002). To date, value added by investors has primarily been found at the point of investment selection or the monitoring of firms as they grow. Given that the majority of entrepreneurial firms fail, establishing that investors can value by replacing founders represents a novel contribution. Our work is also related to the “horse-vs-jockey” debate in venture capital. Among firms that completed an IPO, Kaplan, Sensoy, and Strömberg (2009) found substantial replacement of CEOs. We likewise find a connection between founder replacement and subsequent liquidity events, but in a large sample of firms with a range of exit outcomes. Our findings suggest that investors find it productive to replace the “jockey” when they believe the underlying “horse” to be of good stock. Finally, our results speak to the tension between maintaining a founder-friendly reputation and optimizing for the performance of the current portfolio. Entrepreneurs care about their expected financial return but also about keeping their jobs. Investors’ aggressive replacement of founders may optimize the performance of the current portfolio, as our results suggest. But developing a reputation as having little patience with founders could also scare off founders—including some of the most highly able founders—who insist on remaining in control of their ventures. Although we do not measure the impact of maintaining a founder-friendly reputation on the ability to attract future entrepreneurs, and suspect that such analysis is not straightforward, our results indicate that not replacing founders is hardly costless. Future work is required to explore this tension. We recognize the support of the Kauffman Junior Faculty Fellowship. We thank John Bauer, Russell Beck, David Denis, and Matthew Rhodes-Kropf; the participants at the Duke Strategy Conference, Duke Finance department, Georgia Tech strategy department, the Northeastern entrepreneurship department; and the NBER Entrepreneurship Working Group for their comments. The VentureSource data were provided by Correlation Ventures, to which Ewens is an advisor and investor. Supplementary data can be found on The Review of Financial Studies Web site. Footnotes 1 See Hellmann and Puri (2002), Sorensen (2007), Hsu (2006), Bottazzi, Da Rin, and Hellmann (2008), and Chemmanur, Krishnan, and Nancy (2011). 2 The data were graciously provided by Correlation Ventures, a quantitative VC fund. 3 The second condition excludes firms that strictly raise capital from angel investors, hedge funds, or corporations. 4 The numbers correspond to exit outcomes from still private firms; the check was performed in April 2017 using the online search capability of both VentureSource and Pitchbook. 5 Founders, by definition, joined at the start date of the firm. 6 We lose 169 firms and 390 founders based on this rule. The firms and founders exhibit no difference in major observables studied. 7 Section A.2 in the Online Appendix has more details on this aspect of the data collection. 8 It may be that an investor remains on the board even after they stop investing in the startup, even if a new investor takes a board seat, so our count of investor-directors may be conservative. 9 The noise inherent in assigning exits dates to board seats leads to some large boards. In the raw data, fewer than 3% of boards have more than ten outside board members; however, these boards are composed of members who are listed as “former” but do not have an exit date. We truncate the outside board size at ten to remove some of this measurement error. 10 Bernstein, Giroud, and Townsend (2016) consider a dependent variable that is one if an IPO or acquisition with at least $25m exit value occurs. Our results are robust to measures of one to three times the exit value to total capital raised. 11 If an acquisition value is unreported, Puri and Zarutskie (2012) suggest that it is small. 12 The results are robust to using the median of the 6- to 9-month market capitalization of firms that had an IPO to account for the lockup period. 13 The financing year is excluded because we have one observation per startup and no event to use for selecting a financing year. 14 In unreported results, we note a strong reduced-form correlation between founder replacement and the number of acquisitions within the same industry two years prior. The two-year lag stems from a “golden handcuffs” contract commonly employed by acquiring firms for the acquired firm’s executive teams. These contracts often involve two- to four-year vesting or bonuses for the executives of acquired firms. Although the stock options of the executives in the target company fully vest on the change of control, incentives are typically added to retain key personnel beyond the acquisition, including large cash-based incentives which are evaluated no later than two years after the acquisition. Because two-year lagged acquisitions might correlate with the current exit market (e.g., merger waves), we do not use this as an instrument. 15 For further details, see Grant and Steele (1996). 16 “Blue-pencil” differs from the “red-pencil” reformation in WI in that blue-pencil allows a judge not just to strike but to rewrite objectionable parts of the contract. For example, if the non-compete is written for a duration of five years, under blue-pencil the judge can simple change the length to one or two years. 17 See also http://tradesecretstoday.blogspot.com/2011/03/failing-to-trust-public-process-of.html. 18 New York and New Mexico also weakened enforceability of non-compete agreements during our sample. The New York reform was specific to workers in the broadcasting industry which is not highly relevant to venture capital activity. Similarly, the reform in New Mexico was specific to physicians. Neither is included in our analysis. 19 The full political economy surrounding the change in Oregon is described in Rasses (2009). 20 The audio of the representative’s proposal of the new law is available at http://www.gencourt.state.nh.us/senateaudio/committees/2012/Commerce/HB%201270.asx 21 We repeated this exercise with population instead of the count of public firms and found even stronger evidence of home bias (though we think the number of public firms a better proxy for the availability of attractive executives). The above exercise confirms that startups are sensitive to changes in non-compete enforceability when hiring replacement executives. 22 Because we have a binary endogenous variable, the first stage is a probit estimator following Wooldridge 2010. From this, we gather the predicted probabilities, which we use as the IV. This approach has the advantage or producing first-stage predictions that are inside the unit interval and the first stage standard errors are correct. The results are qualitatively and statistically similar if each stage is a linear model. 23 The $$R^2$$ are not reported for the second stage because they are not a relevant summary statistic in the 2SLS setting. 24 The Hausman test for whether the 2SLS and OLS differ rejects the null that they are the same. If the IV is indeed valid, this is additional evidence that the replacement dummy is endogenous. 25 Our IV estimator uses the first stage predicted probability from a probit following Wooldridge (2010) so we have to run each as a separate regression. 26 Like in the case of the incoming replacement, whether the founder stays or leaves after being replaced may be determined by investor preference and founder preference. Investors may insist that founders depart upon replacement, or founders may decide to leave post-replacement even if investors try to retain them in a different role. As noted earlier, replaced founders who stay have less work experience and fewer master’s degrees but are more likely to have a PhD. 27 In all of the states in which enforceability was strengthened by the legislature—Florida, Idaho, Georgia, Arkansas, and Alabama—continued employment suffices as a consideration for a non-compete. 28 Note that the sample is different in each of these alternative specifications because dropping a treated state also leads to a loss of some VCs whose portfolios form the samples. 29 The limited evidence to date regarding the effect on startup hiring of non-compete agreements is moreover mixed. The only paper we are aware of in this vein is Starr, Balasubramanian, and Sakakibara 2015, who finds no effect of non-compete agreements on employee growth for the vast majority of startups. 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The Review of Financial StudiesOxford University Press

Published: Apr 1, 2018

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