Personal Wealth, Self-Employment, and Business Ownership

Abstract

We study the effect of personal wealth on entrepreneurial decisions using data on mineral payments from Texas shale drilling to individuals throughout the United States. Large cash windfalls increase business formation by 0.8 to 2.1 percentage points, but do not affect transitions to self-employment. By contrast, cash windfalls significantly extend self-employment spells, but do not affect the duration of business ownership. Our findings help reconcile contrasting findings in prior work: liquidity constraints have different effects on entrepreneurial activity that may depend on the entrepreneur’s motivations.

Liquidity constraints have long been thought to be a crucial barrier to entrepreneurship (see e.g., Evans and Jovanovic 1989). Despite significant academic attention, the empirical evidence on the role of liquidity constraints is inconclusive. Early work sought to test this link by relating entrepreneurial decisions to wealth from inheritances (see, e.g., Holtz-Eakin, Joulfaian, and Rosen 1994; Blanchflower and Oswald 1998). However, drawing causal inference between wealth and entrepreneurship has been challenging because wealth shocks can correlate with other factors that drive business formation (Hurst and Lusardi 2004). More recently, the literature has studied shocks to households’ liquidity through their access to credit markets. Yet, more access to credit has been found to have positive effects, negative effects, or no effect at all (Dobbie, Goldsmith-Pinkham, Mahoney, and Song 2020; Bos, Breza, and Liberman 2018; Herkenhoff, Phillips, and Cohen-Cole 2021). Given these ambiguous findings, how liquidity constraints affect entrepreneurial decisions remains an open question.

This paper makes two contributions to our understanding of how liquidity constraints relate to entrepreneurial decisions. First, we introduce a new set of individual wealth shocks that makes progress on the identification challenges faced in prior empirical work. Specifically, we collect data on cash windfalls paid to individuals from shale natural gas extraction. Conditional on owning mineral rights, the size of the windfall is difficult to anticipate and is driven by factors outside of the individual’s control, such as the timing and extent of exploration by extraction companies. Thus, our identification strategy is to compare entrepreneurship choices (both self-employment and business formation) for individuals who receive large cash windfalls (e.g., |$>$|

50,000) versus smaller or no windfalls. Second, we use detailed credit profile information to study how the effects of cash windfalls differ for two types of entrepreneurial activities—self-employment and business formation—that prior work has tended to study independently. Using these comparisons, we develop insight into how liquidity constraints affect entrepreneurship, including why prior work has produced a range of conflicting findings.

Our main results show that the impact of personal wealth on entrepreneurial activity critically depends on how entrepreneurship is measured. Our setting permits us to distinguish the effects of personal wealth on self-employment from the effects on business ownership. Recent survey evidence supports the interpretation that the formation of an incorporated business is more closely linked to Schumpeterian growth, whereas self-employment reflects less growth-oriented pursuits, such as subsistence work and a preference to be one’s own boss.¹ Though the survey literature identifies distinct types of entrepreneurial activity, many attempts to estimate the effect of wealth on entrepreneurship do not distinguish these two, often because of data limitations (see, e.g., Bos, Breza, and Liberman 2018). We observe striking differences by entrepreneur type when we draw the distinction between self-employment and business formation. For example, personal wealth shocks greater than

50,000 increase business formation by 0.8 to 2.1 percentage points, but these same wealth shocks do not spur new self-employment spells. Viewing these results together, wealth shocks can increase entrepreneurship but the positive effects are for the formation of incorporated businesses in which liquidity constraints are more likely relevant.

We also test whether cash windfalls affect the likelihood of remaining in self-employment or business ownership. We find that cash windfalls significantly extend preexisting self-employment spells. Conditional on being initially self-employed, those receiving large cash windfalls (⁠|$>$|

50,000) are 16.2 percentage points per year more likely to remain self-employed. By contrast, wealth shocks do not affect the duration of business ownership beyond the initial entry decision. Combined with the results on entry, the impact of wealth shocks on self-employment versus business ownership are quite distinct, which suggests one reason why prior work obtains conflicting findings.

Our setting and additional tests provide robustness and credibility to these results. First, in using shale royalty payments to individuals, our results rely on variation in personal wealth that the individual receiving the payment has no control of. In our most refined specification, we compare individuals who both received payments, but one received a large payment versus another received a small payment, holding constant the parcel size of mineral acreage. Second, for each of our main results, we perform a specification curve analysis (proposed by Simonsohn, Simmons, and Nelson 2015, and applied in Cookson 2018; Akey, Heimer, and Lewellen 2021), which transparently shows the sensitivity of our conclusions to different specification choices. For 64 specifications that span all the different choices of controls, we find these main results hold across a wide array of potential controls after conditioning on mineral acreage owned. Third, our tests exploit the timing of individuals receiving large payments in a panel difference-in-differences setting. Prior to receiving the first cash payment, individuals are on similar trends, which diverge upon realizing the windfall. Finally, we employ a placebo test where we redefine the treatment group to be individuals who receive small payments (i.e., lower than

50,000, but more than

$\$$

10 with an average of

$\$$

1,922 in payment received). We find that small payments have no effect on both self-employment and business formation.

Next, we turn to economic mechanisms. Our findings on business ownership are consistent with models of liquidity constraints as a barrier to entrepreneurship (e.g., Kihlstrom and Laffont 1979; Evans and Jovanovic 1989; Manso 2016), as well as prior work on financial constraints of existing young firms (Hadlock and Pierce 2010; Robb and Robinson 2014). We find that large cash windfalls spur new business formation but they have no effect on the continuation decision for those who already own a business. These findings support the view proposed by the literature that financial frictions are acute at firm birth, but that they diminish over time.² In this way, our finding that personal wealth does not affect the business exit margin is consistent with conventional corporate finance teachings that business owners should pursue projects with positive net present value, and thus, they should treat unexpected cash windfalls as unrelated to the decision to continue business operations.³

Our findings on self-employment entry and exit contrast with the pattern of results for business ownership. Specifically, we find that wealth has little impact on inducing regularly employed individuals to start new self-employment spells. On the other hand, wealth shocks substantially extend preexisting self-employment spells. These results suggest that self-employment entry and exit dynamics require a distinct conceptual framework relative to business formation dynamics. One potential explanation is that self-employment is akin to a luxury good for those who value its private benefits, an argument put forth in Hurst and Pugsley (2017). Adapting this idea to our setting, we expect that individuals sort into self-employment based on their preference for self-employment because they enter low-scale activities that have few barriers to entry. Accordingly, people who are self-employed (not self-employed) before receiving wealth windfalls place high (low) value on the private benefits of self-employment. Given that peoples’ initial choice reveals how much they value self-employment, regularly employed individuals are unlikely to use personal wealth shocks to enter self-employment, consistent with our finding that wealth shocks do not encourage new self-employment spells. Relating this framework to exits, self-employed individuals extend their spells after receiving wealth shocks because it allows them to be self-employed for longer, appealing to the high value they place on the private benefits of self-employment.⁴ In further support of this idea, we find that individuals who continue self-employment after receiving shale royalties earn lower incomes than those who exit self-employment.

We also evaluate how a larger set of theories may relate to the empirical patterns we observe for self-employment. For example, according to the experimentation view of entrepreneurship (Manso 2016 and Dillon and Stanton 2017), the wealth shock may alleviate a financial constraint that emerges at an intermediate stage of the venture. In this framework, self-employment enables individuals to try out ideas at low scale before injecting capital at an intermediate stage to eventually grow the business idea. Although this is a plausible potential mechanism for why wealth shocks extend self-employment spells, we find no evidence that wealth shocks speed the transition from self-employment into business ownership. Distinct from the experimentation view, behavioral theories, such as the sunk cost fallacy, posit that self-employed individuals might double down on their struggling business ventures when a wealth shock allows it. Such behavior would explain why individuals extend self-employment spells after receiving a windfall, but without additional assumptions about who exhibits the bias, this theory has a more difficult time explaining why windfalls do not also induce business owners to remain in business ownership for longer. In contrast to these alternative theories, the private benefits framework explains why there could be different effects of cash windfalls on business ownership versus self-employment because the framework predicts that individuals sort into these different activities based on their preferences. Namely, individuals with strong nonpecuniary motivations choose low-scale entrepreneurial activities like self-employment, and via this same selection mechanism, people who choose to own an incorporated business tend to be motivated less by private benefits. The sorting across business ownership and self-employment in our setting aligns well with the Levine and Rubinstein (2017) survey evidence that the owners of incorporated businesses are more motivated by business growth. Although the private benefits framework provides a parsimonious explanation for our findings on self-employment and business ownership dynamics, we acknowledge that self-employment entry and exit behavior also might be influenced by these alternative economic mechanisms.

Our paper makes several contributions to the entrepreneurship literature. First, we present contrasting findings for self-employment and business ownership, which offers a novel perspective within the literature that studies entrepreneurship types. Notably, prior work has identified a wide set of motivations that characterize entrepreneurial decisions (e.g., Puri and Robinson 2007; Puri and Robinson 2013; Astebro, Herz, Nanda, and Weber 2014; Hvide and Panos 2014; Lafontaine and Shaw 2016; Kerr, Kerr, and Dalton 2019; De Meza, Dawson, Henley, and Arabsheibani 2019), and has linked these motivations to different types of entrepreneurship (Levine and Rubinstein 2017). From both a survey and theoretical perspective, these studies propose that the most impactful entrepreneurial ventures are found when individuals form incorporated businesses (Hurst and Pugsley 2017). Relative to this literature, the heterogeneous effects of personal wealth windfalls draw a sharp distinction between self-employment and business formation decisions. Beyond differing motivations, our results show that self-employment and business ownership are economically distinct activities that likely respond differently to the same policies.

Our evidence on personal wealth shocks also relates to the empirical literature on barriers to entrepreneurship (e.g., Bianchi and Bobba 2013; Blattman, Fiala, and Martinez 2014; Gottlieb, Townsend, and Xu 2016; Naaraayanan 2019; Hombert et al. 2020). For example, previous work has examined how entrepreneurship is affected by shocks from household balance sheets, and separately, shocks to the broader banking sector (e.g., Black and Strahan 2002; Kerr, Kerr, and Nanda 2015; Fracassi, Garmaise, Kogan, and Natividad 2016; Bernstein, McQuade, and Townsend 2018).⁵ Within this literature, our paper shows how wealth shocks affect entry and exit decisions into self-employment versus business ownership. By contrasting the effects for these distinct types of entrepreneurial activity, our work emphasizes the importance of understanding the competing mechanisms that drive entrepreneurial activity (e.g., initial liquidity constraints vs. preferences for entrepreneurship).

Further, we contribute to the understanding of the impacts of personal wealth windfalls on entrepreneurial decisions.⁶ Specifically, our study of the impact of cash windfalls from shale most closely relates to prior and contemporaneous work (e.g., Cespedes, Huang, and Parra 2019; Mikhed, Raina, and Scholnick 2019; Bermejo, Ferreira, Wolfenzon, and Zambrana 2019).⁷ In this respect, Lindh and Ohlsson (1996) uses data from Sweden to argue that winning the lottery results in increasing transitions into self-employment. However, even within the setting of Swedish lotteries, Cesarini et al. (2017) find opposing results, and attribute the difference to the fact that they control for the number of lottery tickets purchased. The analogous feature of the shale windfall setting is to control for the amount of mineral acreage, as we do in all of our empirical tests. In this way, our paper makes an identification contribution, which helps us to resolve inconsistencies in the literature. Another distinguishing feature of our setting is that we study a broad sample of individuals in the United States, which is not necessarily representative, but combined with the insights of prior literature, our results help to complete the picture of how wealth windfalls matter.

1. Setting and Data

1.1 Overview of Barnett Shale and mineral rights

Our study focuses on a sample of oil and gas mineral owners with claims to mineral extraction in the Barnett Shale of Texas from 2010 through 2015. The Barnett Shale was the first shale gas development in the United States. Before the mid-2000s, shale gas had been uneconomic to drill and develop. However, the combination of horizontal drilling with hydraulic fracturing (“fracking”), by Devon Energy and George Mitchell, led to a technological breakthrough which allowed vast new quantities of natural gas to be developed. According to the U.S. Energy Information administration, shale gas production was less than 1|$\%$| of total U.S. natural gas production in the year 2000, but by 2015 accounted for 46.2|$\%$| of total U.S. gas production. Moreover, the Barnett Shale was the first shale development in the United States. It was also among the most prolific: the four Barnett Shale counties in our analysis accounted for 17.3|$\%$| of total U.S. shale gas production when shale production peaked in 2012. We start in 2010 largely because that is the first year in which we can construct panel data with detailed work status and business ownership information. Even after development in the Barnett Shale begins, timing of payments and quantities are challenging for mineral owners to determine. Moreover, our main specifications provide results that focus on mineral owners that have similar sized mineral tracts (similar exposure to the shock), but ended up having different quantities of natural gas produced. In the context of our empirical design, Section 2.3 provides evidence that individuals did not anticipate the payments they would eventually receive (even after 2010); we find parallel trends in self-employment rates between those who receive large windfalls against our control samples.

Who owns mineral rights in the United States? These rights typically reside with individuals whose families were involved in the initial permanent settlements of oil and gas producing regions of the United States. The mineral rights were then often severed from surface rights when those families migrated elsewhere. According to news articles and other anecdotes about mineral ownership, the discovery of shale and the resultant wealth shock was largely unexpected by individual recipients. For example, the following characterization published by Kiplinger’s Magazine is relatively common:

“Pam Cooner, 42, an occupational therapist in Houston, has collected about

$\$$

15,000 in the past year for a fractional ownership of mineral rights. Cooner was surprised when contacted by a landman about the rights. She didn’t know she’d inherited them—as had 13 other distant family members. In August, Cooner got a

$\$$

400 royalty check for rights on another property, owned jointly with a different, nonfamily group—again, a total surprise.”

For those fortunate to own minerals, which typically occurred through family ancestry, the shale breakthrough caused the mineral rights, previously a deep out-of-the-money option, to become a valuable cash-flow stream when natural gas was drilled. Therefore, although people who own minerals are not a purely random sample of U.S. individuals, the increase in personal wealth these mineral owners experience was due to an exogenous technological breakthrough over which these individuals did not have control. Figure 1 presents the geographic distribution of individuals who receive mineral payments in our sample.

1.2 Oil and gas lease and royalty data

When an oil and gas firm decides to drill and develop an oil and gas reservoir, it must first negotiate a contract, often with a private individual for the right to do so. These private individuals constitute our sample of royalty recipients. Contracts to develop oil and gas compensate a mineral owner in two ways. First, prior to any extraction, a mineral owner will receive an upfront bonus payment, which typically will be a dollar per acre value. For example, a person receiving a

5,000 per acre bonus that owns 10 net mineral acres would receive a check for

$\$$

50,000. Second, once extraction commences, individuals receive a royalty stream based on their share in a well. In our sample, royalty percentages range from 12.5|$\%$| to 30|$\%$|⁠, with 18.75|$\%$| being the most common. An individual’s dollar royalty payment is also scaled by their interest percentage in a drilling unit. In Texas, the law is such that royalties are computed based on gross revenues, and no costs can legally be deducted from the gross revenue. For example, if a well generates gross revenue of

$\$$

10,000 in a month, and an individual owns 10 net mineral acres at a 20|$\%$| royalty on a 400-acre drilling unit, that individual would receive a check for

$\$$

10,000*10/400*20|$\%$| =

$\$$

50 for that month.

Accurate data on payments that individuals receive is difficult to obtain and compute. Fortunately, in the state of Texas, unlike in other states, mineral owners are required to pay property tax. Texas requires all oil and gas firms to turn over their so-called “pay decks” with detailed well-by-well ownership interest information to the state. We use this royalty interest information to compute an ownership value based on the production profile of each well. Because property tax information is public information in the state of Texas, we used open record requests to obtain the detailed title and ownership information that private firms paid millions of dollars to construct. The data are provided in PDF format, which required us to convert the images into usable data. In our study, we focused on compiling mineral appraisal roll data for the four main producing counties in the Barnett Shale going back to the year 2010. Though shale drilling eventually expanded to states outside of Texas, the identities of individuals who own mineral rights to oil and gas wells in other states is not easily attained. Public county court records can be used to compute ownership percentages, but this often requires manually searching county indexes and filings, and oil and gas firms typically pay an average of

50,000 per well to compile accurate royalty owner information from these public records. To put this in perspective, we note that our sample comprises 7,041 wells.

A crucial feature of our mineral roll appraisals is that they provide the address at which each mineral owner receives tax bills. This accurate address is useful for ensuring a high-quality merge with credit bureau data. Furthermore, we used the well ownership percentages to calculate individuals’ royalty payments. To do so, we matched these percentages with well production and natural gas pricing. For each well in our sample, we compile monthly production data from the oil and gas regulatory body in Texas, namely, the Texas Railroad Commission. We then multiply production by prevailing spot natural gas prices reported by the U.S. energy information administration for a given month, this computation gives us the total gross revenue of a well, which combined with ownership information from the mineral rolls, is sufficient to calculate the amount of each individual check.

In our sample, royalty payments from production account for 60|$\%$| of total payments. The remaining payments are the bonus payments that mineral owners received at the time a lease was signed. To compute bonus payments, we conducted public record requests for all oil and gas leases from the four counties in our study, as well as county indexes. The lease bonus payment in many cases is not reported on a lease because it is not required to be. However, many leases do have this information, as well as net acreage amounts. Based on the leases that do have lease bonus information we estimate a regression to predict the lease bonus payment on a dollar-per-acre basis using time fixed effects, county fixed effects, and operator fixed effects. The R-squared we obtain from the regression is .82. We then use this predicted amount to estimate the lease bonus amounts for the remaining sample in which we do not have direct data on bonus payments.

Once we have computed lease bonus payments and royalty payments for the sample, we then merge the royalty payment data and the lease bonus payment data to obtain our overall payment amounts. Overall, the payment that someone receives is a function of prevailing natural gas prices, the amount of net mineral acreage they own, and the amount of natural gas produced on their mineral acreage. Crucially, as shale development increased over time, there was a high degree of spatial heterogeneity in well production. This variation frequently caused individuals to receive vastly different payment amounts, even when these individuals are from the same region and own similar amounts of mineral acreage.

1.3 Experian data overview

We contracted with Experian to merge the mineral rights data with two distinct data sets that Experian maintains: (a) individual-level credit bureau data and (b) business owner credit data.⁸ We provided Experian information on payments, names, and addresses, Experian conducted the merge on name and address, and returned to us the payments data merged with credit bureau data without the personally identifying data fields. In addition, Experian provided us with two control samples, (a) a sample matched on the geography and age distribution of our Experian records and (b) a nationally representative sample. The merge with credit bureau data returned an 80|$\%$| match rate.

1.3.1 Self-employment and business ownership data

Table 1 presents summary statistics on the panel data set for person-year observations in our merged sample (2010–2015). We restrict attention to mineral owners (and their matched controls) who received their first mineral payment after 2010 because this is the earliest year in which we can observe entrepreneurial decisions.⁹ To focus on a consistent sample in the person-year panel, we restrict attention to mineral owners (and matched controls) who received no mineral payments prior to 2011, and for whom we have complete data from 2010 through 2015. These restrictions leave us with a sample of 85,102 mineral owners (74,149 of whom received a cash windfall vs. 10,953 who received no payment despite owning mineral rights) and 85,102 control individuals drawn from the Experian sample. We observe each of the 170,204 individuals in our sample across all six years in our sample, adding up to 1,021,224 person-year observations. In the merged sample, we observe annual snapshots of personal credit bureau characteristics for each individual and business credit characteristics for businesses owned by the individual (if the individual is a business owner). The consumer credit data contain fields that are commonly studied using credit bureau data (e.g., credit score and estimated personal incomes modeled using actual W2 statements), together with a demographics file. Experian provided us with individual-year observations between 2010 and 2015 on two distinct entrepreneurial decisions, self-employment and business ownership. These data are unique to our study. These two variables are the primary outcome variables in our regressions.

We infer self-employment status from a textual field from Experian’s demographics file. This textual field lists the name of the employer of an individual (e.g., “Fort Worth Independent School District”). When someone is self-employed, the textual field is clearly indicated as “self-employed.” Alternatively, an individual who starts a business may choose to incorporate that business, in which case the name of the incorporated business would show up as the employer. Thus, the self-employment measure is unlikely to reflect incorporated entrepreneurship.

To measure incorporated entrepreneurship, we look to Experian’s business credit data. For each individual in our sample, we observe annual snapshots of business credit characteristics from 2010 through 2015 when the individual owns that business. Thus, we observe directly whether someone is a business owner annually between 2010 and 2015 for businesses that have applied for credit, and have an Experian business credit profile. In addition to the requirement that the business applied for credit, the business credit data have a flag that indicates whether the business is incorporated, which we use to ensure that the individual’s business is incorporated. This procedure helps us identify business ventures that are incorporated, which relates to similar classifications in the entrepreneurship literature (e.g., Levine and Rubinstein 2017).

These two measures of entrepreneurial decisions have several properties that validate their use. First, the minimal overlap between self-employed individuals and business owners in our sample confirms that the two measures capture distinct entrepreneurial activities. This can be seen in the subsamples presented in panels B and C of Table 1. For example, conditional on an individual being self-employed in 2010 (panel B), only 3|$\%$| of person-year observations between 2010 and 2015 are business owners. Conversely, if an individual is a business owner in 2010, only 5|$\%$| of person-year observations between 2010 and 2015 correspond to that individual being self-employed.¹⁰ These summary statistics clearly indicate that self-employment and business ownership are distinct economic activities, consistent with similar classifications in the literature (see, e.g., Levine and Rubinstein 2017).

Second, as an external validation exercise, we benchmark the propensity to be self-employed from the credit bureau to two other data sources used in the literature: the American Community Survey (ACS) and Current Population Survey (CPS). To ensure the direct comparability of the samples, we employ our nationally representative sample for these validation exercises. To illustrate this comparison, we plot self-employment propensity at the state-year level and find a high degree of correlation with measures of unincorporated self-employment while obtaining a lower correlation with incorporated self-employment in the public use microdata (see Figure 2). Further, it does not appear to be the case that self-employment is a stand-in for being unemployed. For example, we report a similar comparison between self-employment and unemployment rates (aggregated to the state-year level), and we find that self-employment is actually negatively related to unemployment rates (see the second panel in Figure A.2).¹¹

Third, validating our use of annual updates to the employment fields, we also examine whether the annual rate of job switches matches with other data sets that study flows of employment (see, e.g., Hahn, Hyatt, Janicki, and Tibbets 2017). Specifically, in Figure A.3 in the Internet appendix, we relate the annual job transition rate inferred from Experian’s employment field to the Job-to-Job (J2J) flow data. At the state-year level of aggregation, we find that job transition rates in the credit bureau data have a moderately strong and positive correlation (0.47) with transition rates in the J2J data, and that the baseline rates are similar (with around 90|$\%$| of individuals staying in their jobs annually). Overall, the credit bureau data offer a measure of self-employment consistent with these other data sources at the levels of aggregation in which we can draw the comparison. However, our entrepreneurship fields are useful because they are observable at the individual-year level, and we have linked these entrepreneurial decisions to plausibly exogenous variation in cash windfalls from natural gas extraction.

Fourth, we contextually validate the self-employment measure by manually extracting and classifying the names of the firms that employ individuals who switched to or out of self-employment. Though we can only examine firm names for individuals during their period of regular employment, these jobs provide useful and granular contextual information on the skills and professions for individuals who choose self-employment in our sample. For firms we can classify industry or skillset reliably, the most common industry for switchers is Real Estate, followed by Government, Construction, and Medical. These four categories combined account for over half of the people who transition into or out of self-employment. By contrast, individuals who work for Technology firms account for less than 5|$\%$| of these switchers. This classification exercise provides some additional context on the types of individuals driving the self-employment decisions we identify in our main tests.

Finally, as an alternative check on data validity, we use the textual employment data field to construct a measure of retirement by searching for the string “retired.” Because retirement is a distinct life cycle marker (with a normal retirement age of 65), this variable allows us to verify whether the timing of the employment field is informative. We find that retirement propensities are greater among individuals of typical retirement age, which further enhances confidence in using the textual descriptions to measure self-employment.

When looking at our full sample in panel A of Table 1, the mean self-employment rate of 1.96|$\%$| is somewhat lower than self-employment rates reported in public use microdata (ACS or CPS). The lower self-employment is also present in the nationally representative sample (see the range on the horizontal axis in Figure 2), which indicates that the self-employment measure provided by Experian undercounts some forms of self-employment (e.g., part-time self-employed). The mean business ownership rate is 1.02|$\%$|⁠.

In addition, individuals in our sample have an average income of

54,377, an average credit score of 708, and are 58 years old on average. Consistent with the Levine and Rubinstein (2017) observation that incorporated entrepreneurs are positively selected, the business owner subsample has higher average income (⁠

$\$$

71,151) and credit scores (728) than the self-employment sample (⁠

$\$$

57,280 and 707, respectively). These summary characteristics indicate that our sample tilts slightly toward older individuals who have higher income and higher credit scores. The fact that mineral rights owners tend to be older is likely because mineral rights tend to be inherited, which makes mineral ownership less likely at younger ages. However, Figure 3 shows much more overlap in individual characteristics (i.e., age, credit score, and W2 income) in our sample of mineral payment recipients versus the nationally representative sample drawn from Experian.¹²

1.3.2 Cash windfalls and balancing tests

The variable of interest in our regressions is whether an individual receives a large payment. To provide context for the underlying variation in payments, Figure 4 presents a histogram of total payments received between 2010 and 2015, grouped by

10,000 bins. The distribution is right skewed, with most individuals receiving relatively small windfall amounts. We choose to set

$\$$

50,000 as the cutoff for large payments because this cutoff is consistent with the capital resources required to enter entrepreneurship based on existing literature. Specifically, Robb and Robinson (2014) find that new businesses require on average

$\$$

40,536 of equity capital, and total financial capital of

$\$$

121,000. For individuals receiving payments greater than

$\$$

50,000 in our sample, the median payment is

$\$$

75,000 and the average payment is

$\$$

110,000. Thus, the

$\$$

50,000 cutoff matches closely with the minimum cash windfall needed to overcome liquidity constraints as a barrier to new business formation. Moreover, these cutoffs also have the attractive feature that they are approximately as large as a typical individual’s annual income in the sample. As a robustness test, we also present results based on the alternative cutoff of

$\$$

100,000.

Our identification strategy is to focus on the large windfall recipients as the “treated” sample, and compare their entrepreneurial decisions before versus after their first payment to “control” individuals who received smaller payments or no payments at all. Holding constant the amount of mineral acreage owned, the identifying variation is driven mostly by the large windfall recipient’s luck in owning a mineral parcel that led to a large amount of extraction. This extraction decision is idiosyncratic to the individual mineral owner, and is controlled by the extraction company.

To illustrate our estimation approach, we identify 460 people who received a large cash windfall (⁠|$>$|

50,000) out of 169,101 people who did not own a business in 2010. Of those who received large cash windfalls, 12 formed incorporated businesses during our sample (a business formation rate of 2.609|$\%$|⁠). By contrast, the control individuals who received smaller or no cash payments formed 1,379 businesses (a much lower business formation rate of 0.818|$\%$|⁠). When we look at new self-employment spells, we find that only 0.217|$\%$| of treated individuals entered self-employment by 2015 (1 out of 460), a similar rate of new self-employment spells as in the treatment group (813 out of 166,352, or 0.489|$\%$|⁠). Figure 5 presents these inflow rates with 95|$\%$| error bars. These raw comparisons highlight our main results on inflows into business ownership and self-employment, which we subject to fixed effects that account for potential confounds (e.g., ownership of mineral acreage and different initial income) in Section 3.1.

As discussed previously, control individuals could differ from treatment individuals on a number of observable dimensions. We address this possibility by creating a matched control group for each of our key samples. Specifically, we conduct propensity score matching in which we match on credit score and length of credit history, while we require that matched controls live in the same three-digit zip code as the mineral owner. Based on this procedure, each person in our mineral roll data corresponds to one matched control individual whose information was drawn separately from Experian. Within the set of people who receive mineral payments, our empirical specifications focus on people who receive large payments (⁠|$>$|

50,000) as the “treated” group. Thus, our tests have two kinds of control individuals: matched controls drawn from Experian and individuals from our mineral roll data who received payments smaller than

$\$$

50,000.

Table 2 presents a series of balancing tests that compare the initial characteristics of large payment individuals to each of these control groups. For each comparison, we present the residual differences of means after conditioning on the fixed effects in our tests (“Adj diff” column).¹³ Critically, the adjusted differences account for the amount of mineral acreage owned, which holds constant background factors that could relate to entrepreneurial decisions (e.g., other economic opportunities). Focusing on the full sample comparisons in panel A, we see that, without controlling for background factors, large windfall recipients are older on average (2.7 years older), have higher average incomes (⁠

8,217 higher) and have higher average credit scores (36.2-point difference). These differences are similar if we focus only on the subset of control individuals who received small payments: 4.7 years difference in age,

$\$$

6,045 difference in income and a 27.1-point difference in credit score. However, for both control samples, the adjusted differences become economically small and statistically insignificant after including controls and fixed effects to focus on the idiosyncratic variation in cash windfalls. For the initially self-employed and business owner subsamples in panels B and C, we see a similar pattern.¹⁴

Our empirical tests in the following section rely on difference-in-differences comparisons of individuals receiving large cash windfalls versus matched controls. To account for any further observable differences between these samples, we additionally include individual fixed effects throughout the panel data sets in our main specifications. Nevertheless, the specification analysis in Section 4.1 shows that their inclusion does not meaningfully affect our conclusions.

2. Main Results

In this section, we present our findings on the effect of large cash windfalls on entrepreneurial decisions. First, we examine the impact of windfalls on inflows into entrepreneurial activity in Section 3.1. For these tests, we restrict attention to the subsample of individuals who are not self-employed or who are not business owners in 2010. Next, we study the effect of windfalls on flows out of entrepreneurial activity in Section 3.2. For these outflow tests, we restrict our analysis to subsamples of individuals who are either self-employed in 2010 or business owners in 2010.¹⁵ Taken together, these analyses show how shocks to personal wealth affect the decisions to enter and exit from entrepreneurial activity.

2.1 Inflows into entrepreneurial activity

Our tests focus on variation in payments outside of the individual’s control. Specifically, we condition on the amount of mineral acreage owned by individual |$i$| by controlling for acre quintile x year fixed effects. In addition, our tests exploit the panel structure to flexibly account for person-level heterogeneity and heterogeneity by geography. The main specification includes a set of granular fixed effects: individual fixed effects, age x year fixed effects (using dummies for each year of age), ZIP3 x year fixed effects, income quintile x year fixed effects (based on, 2005, preshock income levels), credit score centile fixed effects, and time-varying controls for common household balance sheet characteristics (⁠|$\mathbf{X}_{i,t}$|⁠).¹⁶ In this specification, therefore, the residual variation in payments is entirely driven by factors external to the individual, that is, the timing and intensity of drilling, as well as macro fluctuations in the price of natural gas.

Table 3 presents the results from estimating Equation (1). In panel A, which focuses on inflows into self-employment, we estimate a small negative impact of receiving a large cash windfall on the flow of individuals into self-employment. For the specification with |$Large\;payment_{i}(>\$50k)$|⁠, the estimated impact of receiving a large payment is to slow the transitions into self-employment by 0.232|$\%$| per year. Though the negative estimate does not square with the motivating economic intuition, the estimate is statistically insignificant and sensitive to the specification employed. For example, changing the shock variable to |$Large\;payment_{i}(>\$100k)$| yields a statistically significant estimate. As columns 3 and 4 show, these conclusions are virtually identical when focusing on the subset of individuals who received mineral payments, and thus, the controls were “unlucky” individuals who received small payments despite owning minerals. Given the nonrobustness and statistical insignificance of these estimates, we interpret the estimates from panel A as a (noisy) nonresult for inflows into self-employment.

In panel B, we consider business formation decisions by replacing the dependent variable with an indicator for business ownership. In contrast to the self-employment specifications, we estimate a positive impact of large cash windfalls on inflows into business ownership. For the specification with |$Large\;payment_{i}(>\$50k)$|⁠, the estimated impact of receiving a large payment is to increase the rate of business formation by 0.897|$\%$| per year, which is quite large relative to the baseline rate of 0.420|$\%$|⁠. Replacing the treatment indicator with |$Large\;payment_{i}(>\$100k)$| leads us to obtain even larger estimated magnitudes: receiving a large payment increases the business formation rate by 2.027|$\%$| on average. These estimates are statistically significant at the 10|$\%$| level, and robust to choices of sampling frame (within the treated vs. full sample).

2.1.1 Heterogeneity

In this section, we examine several dimensions of heterogeneity in the effect of personal wealth on entrepreneurial activity. Table 4 presents the results from estimating Equation (1) after sorting the data into subsamples based on the individuals’ incomes before receiving shale royalties. We estimate heterogeneity in the effect of cash windfalls by individuals’ initial incomes because, according to conventional theories of liquidity constraints, a positive wealth shock should have a larger effect on those who are initially more constrained (i.e., individuals who have lower incomes prior to the shock). For inflows into self-employment and business ownership, the main takeaway from this table is that the impact of cash windfalls is not significantly different for high income individuals versus low-income individuals. That is, the differences between low-income versus high-income samples are statistically insignificant and sensitive to the specification choices.

Similar to the heterogeneity by initial income, we also examine whether the effects of cash windfalls are more pronounced by different age and education categories.¹⁷ Panel A of Figure 6 presents the result from allowing the effect of personal wealth to be different for younger people versus older people, splitting by the median age of 58. Although these estimates have larger standard errors, the estimated effect of cash windfalls is similar for young and old individuals, indicating that the relatively old composition of our sample does not explain our findings. In a similar vein, panel B of Figure 6 presents the result from allowing the effect of personal wealth to differ for college graduates versus people who have not attained at least a college diploma. We find similar effects for low-education versus high-education individuals, which are similar to the findings we present based on the overall sample. These heterogeneity exercises show that our findings are not driven by particular segments of our sample.

2.2 Flows out of entrepreneurial activity

In these specifications, we condition the sample on individuals who were entrepreneurs at the beginning of our sample in 2010, which implies that the coefficient of interest |$\beta_{1}$| reflects the difference in rate of flowing out of entrepreneurship between (treated) individuals who receive large payments versus (control) individuals who do not (before vs. after the date when the individual receives the first mineral payment). We cluster standard errors at the individual level.

Our tests focus on variation in payments outside of the individual’s control. Specifically, we condition on the amount of mineral acreage owned by individual |$i$| by controlling for acre quintile x year fixed effects. In addition, our tests exploit the panel structure to flexibly account for person-level heterogeneity and heterogeneity by geography. The main specifications include a set of granular fixed effects: individual fixed effects, age x year fixed effects (using dummies for each year of age), ZIP3 x year fixed effects, income quintile x year fixed effects (based on 2005 preshock income levels), and time-varying credit score centile fixed effects. In this specification, therefore, the residual variation in payments is driven entirely by factors external to the individual, that is, the timing and intensity of drilling, as well as macro fluctuations in the price of natural gas.

Table 5 presents the results from estimating Equation (2). In panel A, which focuses on flows out of self-employment, we estimate a large and significant negative impact of receiving a large cash windfall on the flow of individuals into self-employment. For the specification with |$Large\;payment_{i}(>\$50k)$| in column 1, the estimated impact of receiving a large payment is to slow the transitions out of self-employment by 16.16|$\%$| per year, which is a large effect relative to the baseline rate of approximately 88|$\%$| of this subsample remaining in self-employment. This estimate is statistically significant at the 1|$\%$| level and is robust to choices of how to model the shock, as well as sampling frame. For example, changing the shock variable to |$Large\;payment_{i}(>\$100k)$| yields a statistically significant estimate of |$-26$||$\%$|⁠. As columns 3 and 4 show, these conclusions are similar when focusing on the most refined sample of individuals who received mineral payments, which uses only variation in whether an individual received small versus large payments.

In panel B, we consider decisions by existing business owners by focusing on the subsample of individuals who owned a business at the start of our sample in 2010. In contrast to the self-employment specifications, we estimate a positive impact of large cash windfalls on flows out of business ownership. This estimate is nonrobust and sensitive to sampling decisions employed. For the specification with |$Large\;payment_{i}(>\$50k)$|⁠, the estimated impact of receiving a large payment is to increase the rate of transition out of business ownership by 4.7|$\%$|⁠, which is relatively small in comparison to the self-employment estimates.¹⁸ These conclusions are qualitatively similar when we restrict attention to the sample of mineral owners who received payments. Given the nonrobustness of the estimates and the small sample size, we are cautious about offering strong conclusions about how wealth affects the flow out of business ownership.

One potential channel for the different effects of wealth on outflows from self-employment versus business ownership is that large windfalls may enable individuals to retire, and this effect could be different for self-employed individuals versus business owners. To evaluate this possibility, we estimate how outflows differ for people above- versus below-median age. Specifically, we estimate Equation (2), but as a triple difference specification that also includes an interaction term |$Post\times Large\;payment$| and an indicator for the individual being below the median age. We present the estimated effects from this specification for above-median age versus below-median age graphically in Figure 7.¹⁹ We observe no meaningful economic differences for young people versus older people in how cash windfalls affect the propensity to remain in business ownership or self-employment. Specifically, we find that wealth extends periods of self-employment irrespective of whether the individual is young or old. Also, consistent with our main set of interpretations, we find no significant effect of wealth on the propensity to remain in business ownership, and this effect is indistinguishable from zero for both young and older individuals.

2.3 Parallel trends

We employ carefully chosen fixed effects to absorb differences across treatment and control groups, including granular controls for mineral acreage owned. Conditional on these fixed effects, we saw that the treatment and control samples were similar on observable characteristics (see, e.g., Table 2). However, an important additional consideration is whether our treatment (high payment group) and control (low payment group) have differential trends in entrepreneurial decisions, which would confound the interpretation of our main difference-in-differences tests.

We explicitly evaluate this parallel trends assumption for the two tests in which we obtain a robust and statistically significant result, that is, the increase in business formation (Table 3, panel B) and the decrease in exit from self-employment (Table 5, panel A). Specifically, for these specifications, we examine the propensity to be self-employed or a business owner in event time (time t = 0 is the year the first payment is received), and plot the estimated coefficients for |$large\text{_}payment(>\$50k)$| times lead and lag indicators in an event window around the year the individual receives the first cash payment. Figure 8, panels A and B, presents these dynamic plots. In both figures, we see nonsignificant estimates prior to the event date, with a significant effect emerging after the first payment date, a pattern that supports the parallel trends assumption.²⁰

Beyond parallel trends, these dynamic specifications restrict attention to the subsample of individuals who received mineral payments, focusing only on the variation in whether an individual received a large windfall (⁠

50,000 or more) versus a smaller windfall. Because the estimates also condition flexibly on the amount of mineral acreage owned, the identifying variation comes purely from mineral owners who were lucky to own minerals that had significantly more natural gas extraction tied to them.

3. Mechanisms and Robustness

3.1 Robustness to specification choices

The main specifications (Tables 3 and 5) include a large number of specification choices. Particularly given the potential small sample size, it is important to evaluate sensitivity to the choices about which controls and fixed effects to include. To evaluate the sensitivity of our conclusions to varying these sampling choices, we present a specification curve analysis, proposed by Simonsohn, Simmons, and Nelson (2015) and previously applied in Cookson (2018), which presents the estimates from all combinations of specification choices. This analysis is particularly important given that two of our main tests (inflows into self-employment and flows out of business ownership) yield estimates that are not statistically different from zero. In particular, presenting the full range of reasonable specifications is informative of whether the result is a robust nonresult, or if different specification choices could reasonably lead to statistical significance.

We plot specification curves for the estimated coefficient for |$Post_{i,t}\times Large\;payment_{i}(>\$50k)$| for our four main results, and these specification curves are presented in Figures 9 (inflows) and 10 (outflows). The estimates are organized as empirical CDFs of the estimated coefficients, with each point reflecting a different specification choice described by the guide at the bottom panel. In each case, the red triangle indicates the reported specification from Tables 3 and 5 with the full set of controls and fixed effects.

Figure 9 presents the specification curves for inflows into entrepreneurship. Panel A presents the specification curve for the inflow into self-employment. Relative to our main estimate that is slightly negative and statistically insignificant, these findings are highly nonrobust, but all are slightly negative estimates. Depending on specification choices, we estimate that a large cash windfall reduces the inflow into self-employment by 0.1|$\%$| to slightly larger than 0.3|$\%$|⁠. Though the estimate is robust in sign, it is relatively small and statistically insignificant for approximately half of the (reasonable) specification choices.

Panel B of Figure 9 presents the specification curve for inflows into business ownership. As the specification curve indicates, the estimated positive effect of cash windfalls on business formation is quite robust to the choices of which sets of controls to include. All specifications in the specification curve give similar estimates, both in terms of magnitude and in terms of statistical significance.

Figure 10 presents the specification curves for flows out of entrepreneurship. Panel A presents the specification curve for the result on the flow out of self-employment. The main estimate we report |$-16.16$||$\%$|⁠, though large in economic magnitude, is in the middle of the distribution of estimates from all reasonable specifications. Across the specification curve, all of the specifications we consider are statistically significant at the 10|$\%$| level or better, and the estimated magnitude ranges from |$-8$||$\%$| to approximately |$-20$||$\%$|⁠. That is, despite the possible concern with this estimate being from a small sample size, the effect of cash windfalls on extending the duration of self-employment spells is a consistent feature of the sample, such that our conclusions are insensitive to a broad set of specification choices.

By contrast, panel B of Figure 10 presents the specification curve for our results showing that wealth shocks do not affect flows out of business ownership. The positive and statistically insignificant estimate that we report in the outflows specification in panel B of Table 5 is actually one of the largest estimates in the specification curve. Other choices lead to smaller (and sometimes negative) estimates on the effect of cash windfalls on the flow out of business ownership. Taken together with the main estimates we report, this specification curve enhances our confidence of no true effect of cash windfalls on the duration of business ownership.

3.2 Transitions from self-employment to business ownership

In this section, we examine the impact of cash windfalls on transitions from self-employment to business ownership. This analysis is of interest because previous work (see, e.g., Dillon and Stanton 2017) has argued that self-employment spells are a trial period in which constrained entrepreneurs learn about their prospective business ideas before forming incorporated businesses. Thus, the subset of initially self-employed individuals is a useful subset to evaluate the impact of shocks to wealth.

Table 6 presents our results on the impact of wealth shocks on the transition rate from self-employment to business ownership. Broadly, we find little evidence that these shocks speed the transition from self-employment to business ownership. Specifically, the only specification with statistical significance for the wealth shock (column 2) indicates a reduction in the transition rate between self-employment and business ownership. As a complement to our main specifications, these findings reinforce our interpretation that self-employment and business ownership are economically distinct activities. Moreover, these results contrast with the idea that self-employment represents a precursor or trial period to business ownership.

3.3 Placebo exercises

An important limitation of our sample is that we have only 6 years of panel data. Thus, the pretrends analysis that we present in Section 2.3 cannot rule out longer-term trends that are changing beyond this window of time. Our paper addresses this concern by presenting a series of placebo exercises for the main specifications.

For the placebo exercises, we estimate the main specifications in which we replace the large payment indicator (⁠|$>$|

50k) by an indicator for a small payment (i.e., individuals who received less than

$\$$

50,000 but more than

$\$$

10 which is equivalent to a windfall of

$\$$

1,922.101 on average). Appealing to the startup capital evidence in Robb and Robinson (2014), these small windfalls are insufficient to affect business incorporation decisions, and thus, provide a useful set of events to use for placebo treatments. Across specifications, we find little impact of small cash windfalls on entrepreneurial decisions. As an illustration of these findings and how they compare to our main results, the dynamic graphs we described in our analysis of parallel trends (depicted in Figure 8) overlay the estimated impact of small windfalls in light gray. Similar to our main findings, we see no parallel trends in the impact of small windfalls, but importantly, we see no significant post effect on either inflows into business ownership or outflows from self-employment. Together with our evidence from the specification curve analysis, these placebo exercises reinforce the interpretations of our main tests.²¹

3.4 Impact on self-employment income

As a final set of evidence on mechanisms behind our main results, we present evidence on how the average income of self-employed individuals changes after receiving large cash windfalls. The motivation for including this test on entrepreneurial incomes is to relate to the literature on the role of nonpecuniary benefits of entrepreneurship. Relating to this idea, Hurst and Pugsley (2017) develop a model of entrepreneurship choice that incorporates a role of nonpecuniary benefits to drive decisions to enter and stay in self-employment. They argue that self-employment is more likely to be driven by nonpecuniary benefits than business ownership. Our results on flows out of self-employment are consistent with this interpretation, but admit other plausible interpretations.

For this reason, we evaluate what happens to the income of individuals who remain in self-employment after receiving a large cash windfall. In Figure A.5 in the Internet Appendix, we present the dynamic graph of the effect of receiving a large cash windfall on the average income for the individuals who stay in self-employment in a triple difference-in-differences. We find that, consistent with the nonpecuniary motives theory of Hurst and Pugsley (2017), individuals who stay in self-employment have lower income (on the order of

150 several years after receiving the first mineral payment). Although this particular result admits alternative interpretations (e.g., the literature suggests that average income is lower for entrepreneurs who value right tail entrepreneurial outcomes), this finding in combination with the main findings on flows into and out of self-employment versus business ownership is consistent with theoretical predictions about entrepreneurs motivated by factors other than income (e.g., Hurst and Pugsley 2017).

4. Conclusion

The economics literature has long understood that entrepreneurship is fundamental to long-term growth (Schumpeter 1934; Parker 2009). Rooted in this understanding, a classic question is to understand what factors hold back entrepreneurs (Evans and Jovanovic 1989), yet the empirical literature on barriers to entrepreneurship has come to mixed conclusions (e.g., Dobbie, Goldsmith-Pinkham, Mahoney, and Song 2020; Herkenhoff, Phillips, and Cohen-Cole 2021; Hombert et al. 2020; Lindh and Ohlsson 1996; Lindqvist, Östling, and Cesarini 2020). In this paper, we provide new insight by studying how different types of entrepreneurs—business owners versus self-employed individuals—respond to wealth shocks. Our core insight is that the effect of household liquidity constraints critically depends on the type of entrepreneurship.

Specifically, using large cash payments to mineral owners for identification, we find that personal wealth spurs on new business formation, but not new spells of self-employment. In addition, these cash payments have no impact on the duration of business ownership while extending existing spells of self-employment. Our work highlights important economic differences between business ownership and self-employment, which provides a new perspective on the wide range of entrepreneurial decisions identified in prior surveys (Hurst and Pugsley 2011; Levine and Rubinstein 2017). These findings suggest that business owners are more disciplined in evaluating the continuation value of their business than are self-employed individuals, a finding that is consistent with the stronger nonpecuniary motives of self-employed individuals noted in the literature (Hurst and Pugsley 2017).

Beyond economic mechanisms, understanding the effects of wealth on entrepreneurial activity is important from a policy perspective. For example, entrepreneurship policies differ with respect to whether they target entrepreneurial constraints directly or depend on direct cash transfers (see, e.g., Howell 2017). Broader policies that consider large transfers of wealth, such as a universal basic income, may also have unintended effects on entrepreneurial activity. In this context, our results suggest that personal wealth is particularly useful for spurring new business creation, whereas it has minimal effect on new self-employment spells. This core finding may inform policies that either insure against downside risk or alleviate financial constraints directly via the banking sector. Though a systematic comparison of policy options is beyond the scope of our study, our core insight that unrestricted cash windfalls have different effects on business formation versus self-employment is important to keep in mind when evaluating the benefits to the broader economy.

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.

Acknowledgement

This paper has benefited from suggestions and comments from two anonymous referees, Stijn Van Nieuwerburgh (the editor), Milo Bianchi, Scott Guernsey, Sabrina Howell, Ramana Nanda, Ben McCartney, David Robinson, Christopher Stanton, and Brian Waters. The paper has also benefited from presentations at Arizona State University, Copenhagen Business School, the Federal Reserve Board, Hong Kong University of Science and Technology, Iowa State University, London Business School, Rice University, Texas A&M, University of Amsterdam, University of Colorado – Boulder, University of Houston, University of Iowa, University of Southern California, Washington University at St. Louis, Yonsei University, the 2019 Labor and Finance Conference (Early Ideas Presentation), the 2019 Winter NBER Entrepreneurship Working Group Workshop, the 2019 KWC Lund Conference on Entrepreneurship, the 2019 HEC Entrepreneurship Conference, the 2019 WINDS Conference, the 2020 Yale-RFS Real and Private-Value Assets Conference, the 2020 Midwest Finance Association Conference, and the 2020 ITAM Finance Conference. We thank the following sources for providing funding support for this project: Wharton Dean’s Research Fund, the Wharton Alternative Investments Initiative, the Rodney L. White Center for Financial Research, the Jacobs Levy Equity Management Center for Quantitative Financial Research, the National Bureau of Economic Research Household Finance Working Group and the Sloan Foundation, the Ewing Marion Kauffman Foundation, and the Center for Research on Consumer Financial Decision Making. Supplementary data can be found on The Review of Financial Studies web site.

Footnotes

References