The effects of credit on high school graduation: Evidence from U.S. bank branching deregulation

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The effects of credit on high school graduation: Evidence from U.S. bank branching deregulation Patrick A. Reilly Skidmore College, 815 North Broadway, Saratoga Springs, NY 12866

a r t i c l e

i n f o

Article history: Received 11 October 2018 Received in revised form 27 March 2019 Accepted 25 May 2019 Available online xxx JEL classification: G21 G28 I21 I24 J2

a b s t r a c t Credit markets affect the real economy in multiple ways. This paper utilizes variation in the timing of bank branching deregulation of 39 states between 1970 and 1994 as an exogenous proxy of credit availability to analyze the link between credit markets and educational outcomes. Using CPS data to estimate reduced form models, results indicate a one percentage point increase in the likelihood of graduating high school after bank branching deregulation. Results also suggest heterogeneity of effects over race. The main findings are robust to placebo tests using false deregulation dates. © 2019 Board of Trustees of the University of Illinois. Published by Elsevier Inc. All rights reserved.

Keywords: Bank branching deregulation Credit availability High school graduation

1. Introduction Understanding the far-reaching economic impacts of credit access helps policymakers legislate successfully. However, researchers find it difficult to separate access to credit from other economic conditions. During the 1970s, 1980s, and 1990s, 39 states passed laws that reduced restrictions on where banks were allowed to have branches. This bank branching deregulation (BBD) increased credit availability by allowing commercial banks to consolidate and to compete in a greater geographic area. By using BBD as a source of exogenous variation, economists found a number of (arguably positive) outcomes stemming from increased credit availability. Generally, the results of these studies provide confirmation of expected outcomes. For example, Tewari (2014) finds easier credit reduces mortgage rates and increases home ownership, and Teng Sun and Yannelis (2016) find credit access reduces student loan interest rates, which increases college attendance.1 Rather than confirming expected relationships, identifying secondary or tertiary outcomes of credit access would further demonstrate the

1

E-mail address: [email protected] Actually mortgage rates act as a proxy for student loan interest rates.

far-reaching effects of financial reforms. Therefore, in this paper, I use variation provided by bank branching deregulation timing in a reduced form model to estimate the overall effect of credit access on high school graduation. The current literature identifies a number of outcomes stemming from BBD that may influence the propensity of high school graduation (HSG). First, increases in home ownership (Tewari, 2014) may improve HSG likelihood by reducing the propensity of families to switch school districts (Aaronson, 2000). Second, availability of student loans (Levine & Rubinstein, 2013; Teng Sun & Yannelis, 2016) may increase the efforts of high school students. Additionally, Beck, Levine, and Levkov (2010) find credit access from BBD improved labor markets for the lowest income decile worker (low-skilled labor). This may draw students away from high school (Black, McKinnish, & Sanders, 2005; Evans & Kim, 2006). Section 3 describes the possible mechanisms at length. In related work, both Levine and Rubinstein (2013) and Teng Sun and Yannelis (2016) identify a relationship between BBD and college enrollment. Each paper concludes increased postsecondary enrollment resulting from BBD via improved credit availability. Levine and Rubinstein focus on the effects of BBD on intellectually able but financially constrained individuals. Teng Sun and Yannelis concentrate on financial constraints, use multiple data sets, and find increases in both postsecondary school attendance, completion of

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postsecondary education, and college loans, especially in low- and middle-income families. Impacts on HSG are as (if not more) important than college attendance. First, HSG does not come at such a high cost for students and their families, so any positive impacts are not offset by wealth reductions. Next, the negative consequences of failing to receive a high school diploma are far worse than the negative consequences of failing to attend college. Bridgeland, Dilulio, and Morison (2006) estimate that those dropping out of high school earn $9200 less income per year on average, face greater rates of unemployment, less often report good health, and need/receive more public assistance than graduates. Oreopoulos (2007) reports similar findings. In this paper, I estimate linear probability models using data from the March Current Population Survey (CPS) 1977–1999 to estimate whether or not individuals achieved specific levels of education. Variation in dates of state-level BBD identifies treatment. Results reveal positive impacts of BBD on HSG along with increases in postsecondary attendance and bachelor’s degree achievement. The parameter estimates for postsecondary outcomes are consistent with results from Teng Sun and Yannelis (2016) and Levine and Rubinstein (2013), which suggests data validity. The results provide no evidence of heterogeneity by gender. However, HSG likelihood of nonwhite individuals is not significantly affected by BBD. 2. Background on bank branching deregulation Deregulation of geographic bank branching restrictions is a widely analyzed policy change. Throughout the 1970s, 1980s, and 1990s, states removed geographic restrictions on bank branching. In 1969, 39 states had regulations on intrastate (within-state) bank branching and all fifty states had regulations on interstate (across-state) bank branching. By 1994, every state except Iowa had deregulated their intrastate branching in some form and only Hawaii continued to prohibit interstate bank branching. 2.1. Why restrictions on bank branching? Taxes on bank profits and bank profits themselves were originally a large part of states’ revenues (Sylla, Legler, & Wallis, 1987). Separating banks geographically, especially in an era without electronic banking or modern transportation methods, allowed local banking monopolies to develop. These local monopolies earned greater profits. Therefore, states earned higher revenues with the geographic restrictions. This rent extraction (McChesney, 1987) relationship became less important (to states) overtime as state governments found alternative sources of revenue. Nevertheless, incumbent banks had incentive to lobby state governments to protect their monopoly rents. Thus the rent extraction turned into rent seeking behavior (Tullock, 1967; Krueger, 1974). 2.2. What causes deregulation? Kroszner and Strahan (1999) hypothesize that the status quo changed in the 1970s and 1980s due to macroeconomic conditions, improvements in banking technology, and competition from financial market innovations. These changes combined to reduce the incentive small banks had to rent seek, while increasing incentives for larger banks to lobby for the removal of geographic restrictions on bank branching. Specifically, high nominal interest rates combined with usury law ceilings reduced commercial banks’ rents, particularly rents for small commercial banks. In addition to usury law ceilings, creation of demand deposit substitutes such as money market mutual funds also reduced bank profits. Contemporaneously, increased use

Table 1 Bank branching deregulation dates, by year. State

Year

State

Year

Alaska Arizona California Delaware Washington DC Idaho Maryland Nevada North Carolina Rhode Island South Carolina South Dakota Vermont Maine New York New Jersey Virginia Ohio Connecticut Alabama Utah Pennsylvania Georgia Massachusetts Nebraska* Oregon

<1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 1970 1975 1976 1977 1978 1979 1980 1981 1981 1982 1983 1984 1985 1985

Tennessee Washington Hawaii Mississippi Kansas* Michigan New Hampshire North Dakota* West Virginia* Florida* Illinois* Louisiana Oklahoma* Texas* Wyoming Indiana Kentucky Missouri* Montana* Wisconsin* Colorado* New Mexico Minnesota* Arkansas* Iowa*

1985 1985 1986 1986 1987 1987 1987 1987 1987 1988 1988 1988 1988 1988 1988 1989 1990 1990 1990 1990 1991 1991 1993 1994 1999

Notes: Dates from Amel (1993). * indicates unit banking state. Year indicates when the corresponding state allowed bank branching throughout the state via mergers or acquisitions. <1970 indicates BBD prior to 1970.

of ATMs and credit scores as well as improvements in information technology all benefited large banks disproportionately with respect to smaller banks. In a rent seeking framework, large banks eventually outbid the incumbent small banks causing legislators to pass BBD (Kroszner & Strahan, 2014).2 2.3. The process of BBD BBD was completed in steps. First, intrastate BBD through mergers and acquisitions; next, full intrastate or de novo branching deregulation, and third, interstate BBD.3 This paper, following the literature, focuses on mergers and acquisitions BBD. Mergers and acquisitions allowed Multibank Holding Companies (MBHC) to consolidate their subsidiaries into branches of a single bank. The literature uses the merger and acquisition (M & A) BBD dates for a number of reasons. First, M & A is typically the earliest of the deregulatory steps. Using a later step contaminates the control group with observations affected by M & A BBD. Next, there is a larger variation in policy timing when using M & A BBD. And finally, previous literature finds the greatest effect on other real variables by using M & A dates (Jayaratne & Strahan, 1996; Beck et al., 2010; Levine & Rubinstein, 2013). Table 1 and Fig. 1, using dates from Amel (1993) and Kroszner and Strahan (1999), present BBD dates for each state. 3. Discussion of mechanisms Before discussing the specific mechanisms, one must understand the starting point (BBD increases access to credit) and what

2 Some small commercial banks and thrifts initiated a last ditch loan scheme to cover their losses from high interest rates and regulation. Armed with deregulation and moral hazard created by federal insurance, some Savings and Loan institutions took on very risky assets to make back losses. The failure of these “junk” assets led directly to the Savings and Loan Crisis in the 1980s. See Kroszner and Strahan (2014) or White (1991). 3 See Kroszner and Strahan (1999) for a more in depth explanation.

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Fig. 1. Dates of US bank branching deregulation.

might influence the end result (HSG, or dropping out of high school). The financial liberalization discussed in the last section should improve credit access to firms and families. BBD generates cost savings through economies of scale and passes cost savings to borrowers because of increased competition. So, after BBD, firms and families have more access to credit at lower prices. This is consistent with the current literature. Previous research finds that BBD increased bank competition, which allowed successful, efficient banks to grow (Stiroh & Strahan, 2003; Cetorelli & Nicola, 2006) and profit (Zou, Miller, & Malamud, 2011). BBD increased credit access to both businesses (Krishnamurthy, 2015; Cetorelli & Nicola, 2006) and families (Tewari, 2014; Célérier & Matray, 2019). Regarding the end result, students drop out of high school for a variety of reasons. Rumberger (1983) sorts these reasons into three general categories. (1) School related reasons such as dislike for school, expulsion/suspension, and poor performance. (2) Economic reasons such as desire to work, financial difficulties, and home responsibilities. And (3) personal reasons like marriage or pregnancy. Credit access most likely affects the economic reasons. In total, 20% of dropouts cited economic reasons. This percentage was higher for men who more often left school because of a desire to work or financial difficulties. If there is an increase in credit access, HSG could be influenced by two broad channels: family investment in education and labor demand. The former channel finds families and individuals receiving more access to credit, which relaxes their budget constraints. Greater budgets increase investment in education. The latter channel focuses on lower financing costs to firms. Lower financing costs affect firms’ production technologies. The particular production technology of interest in this analysis is the balance of skilled versus non-skilled labor. Greater demand of low-skilled labor might incentivize leaving school early. The remainder of this section is an in-depth discussion of these channels. 3.1. Family educational investment channels Relaxing credit constraints on families will increase investment in education. For instance, a high school student is forced to work to help his or her family when a parent loses their job. The student’s school performance suffers because he or she is spending so much time working. Eventually, the student drops out of school to work full time. If the family had better access to credit, they might be able to take out a loan while the parent looks for a job. In this case, the student would not need to work as much, if at all, and his or her studies would not suffer.

There are plenty of additional mechanisms related to easier credit access for families. Students may base their effort in high school on the likelihood they can continue their education in college. Relaxing branching regulations increased college attendance through credit availability (Teng Sun & Yannelis, 2016; Levine & Rubinstein, 2013). Credit availability would not affect HSG in the same way. Nevertheless, one may posit that students change behavior based on greater access to postsecondary education. This is unlikely to cause any significant effects on HSG. In order to take advantage of more accessible college education, students must possess the skills to succeed academically. If a marginal increase in credit availability would allow an individual to earn a college degree, then what could be stopping him or her from graduating high school? That is not to say that every high school dropout is incapable of graduating college, but those dropouts who are capable face some constraint. And if they cannot overcome said constraint to avoid dropping out of high school (typically a publicly provided good) then there must be a non-financial constraint or a financial constraint much larger than a marginal increase in credit availability can alleviate. So, even if credit is made more available via BBD, the constraint remains. The child’s age might influence the effectiveness of an increase in credit. Caucutt and Lochner (2012) find differences in returns to educational investment in younger versus older students. They split parental investment on child’s education into “early” (investment in young children) and “late” (investment in adolescents) categories and find early investment is of greater importance than late. Without the early investment, the individual will be of lower ability and cannot take advantage of future educational subsidies. Thus, younger individuals at the time of BBD may have benefited, through improved ability, from increased early educational investment. This may have reduced the overall cost of education, leading to increases in both high school and college attainment. It could be that increased access to college may tarnish the prestige of a high school diploma. Bedard (2001) demonstrates that relaxing credit constraints on high-ability high school students (or their families) enables them to signal those abilities to employers by earning a postsecondary degree. If these high-ability individuals earn a college degree ex post, they reduce the average expected ability level of someone earning a high school diploma. In this case, employers decrease their expectation of ability signaled by high school diploma earners. Thus, firms reduce the relative wage and employment opportunities provided to individuals with high school degrees but no

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college degree. Individuals on the margin will drop out because the relative benefits of graduating high school decrease. Therefore, this theory suggests BBD could reduce HSG.

3.2. labor demand channels BBD has been linked to labor market outcomes. Benmelech, Bergman, and Seru (2011) and Beck et al. (2010) find decreases in unemployment rates following BBD. Results in Boustanifar (2014) demonstrate a positive association between BBD and employment growth. These labor market changes should affect educational attainment.4 Greater educational attainment increases both forgone earnings and future earnings. Therefore, I would expect BBD to cause changes to HSG if BBD benefited a certain skill level of worker relatively more than other skill levels. Specifically, I expect more dropouts (graduates) if BBD disproportionately benefits low-skilled (high-skilled) workers. Beck et al. (2010) provide evidence of disproportionate labor market changes from BBD. They find that BBD raised the income and employment hours of low-skilled individuals. This means increased returns for low-skilled jobs relative to high- or medium-skilled jobs. It follows that, on the margin, individuals would lower educational investment since low-skilled jobs became relatively better paying and more available after BBD. Jerzmanowski and Nabar (2013), however, find opposing results. They find that wages of skilled labor increased and wages of low-skilled labor decreased following BBD. Thus, on the margin, educational attainment would increase as individuals try and earn those heightened wages at high-skilled jobs.

4. Data and methods 4.1. Identification To precisely identify the effects of BBD on HSG, (1) HSG must not influence BBD timing, (2) economic/political situations influencing the timing of BBD cannot affect the propensity of a state’s population to graduate high school, and (3) the timing of BBD must be unrelated to other state/year specific policies that may influence HSG. For example, financial equalization court rulings changes school funding for some states during this time period, however, the timing of these rulings does not correspond closely to the branching deregulations.5 The Community Reinvestment Act (CRA), another potentially confounding policy, went into effect in 1977. The CRA required banks to prove they helped meet the credit needs of their entire community, especially lower income neighborhoods.6 Therefore, banks adhering to the CRA should positively impact poorer communities including education of those community members. Banks in states with fewer bank branching restrictions had greater incentive to adhere to the CRA as compliance is taken into account when approving branching requests. Additionally, having more branching increases the geographic domain of a bank. This increases the likelihood that it serves both poor and wealthy communities, which compels the bank to change its lending to comply. However, the

4 For empirical evidence on how labor market conditions influence HSG likelihood, see Evans and Kim (2006), Black et al. (2005), and Rees and Mocan (1997). 5 See Card and Payne (2002) for dates. 6 See Haag (2000) for a review of the literature on the CRA. Empirical papers identify numerous effects of the CRA such as reduced mortgage lending (Bostic & Robinson, 2004) and increased small business start-ups, which increased employment and economic growth (Kobeissi, 2009).

CRA is unlikely to strongly affect my analysis as it was not enforced with regularity until 1989 (Macey & Miller, 1993).7 Understanding why banks deregulated helps to clarify and assuage endogenity concerns. In part because of the usefulness and popularity of exploiting the timing of BBD as a natural experiment, Kroszner and Strahan (1999) investigate the possible explanations of state specific timing.8 As discussed at length in Section 2.2, they find that the most important factors influencing the timing of BBD are the relative size of the interest groups of the would-be winners and losers of the deregulation. For instance, a state is more likely to deregulate later with a relatively higher proportion of small banks (losers of deregulation). High school graduates (or dropouts) do not share a specific interest in the case of BBD and likely do not pay attention to such legislation. Nevertheless, it is plausible that states where citizens have higher propensities to graduate high school could have a greater presence of winners/losers of BBD. To investigate this issue, Fig. 2 plots BBD timing over the proportion of people in that state that have a high school degree/GED at age 20 in the 10 years leading up to BBD. The lack of any significant relationship mitigates endogeneity concerns. The t-statistic for the simple correlation is −0.08 for the data collapsed to state level and −0.74 for a simple regression of individual level data with standard errors clustered by state.9 4.2. Empirical method The typical approach in the literature uses a state-year panel and implements a difference-in-differences approach based on the timing of BBD. This study differs in several ways, but is similar in its use of BBD dates to identify a treatment group. First, I am not using panel data. I analyze CPS data: cross-sectional, individual level data gathered over a number of years. A more comprehensive discussion of the data follows in Section 4.4. The empirical setup is an intent-to-treat where BBD dates and birth years of the survey respondents are used to identify treated and control groups. Further discussion on treatment follows in Section 4.3. Finally, I estimate linear probability models (LPMs) because of the bivariate nature of the educational attainment variables.10 I estimate the following LPM using ordinary least squares (OLS): Yi = ˛ + BBDi + ˇXi + Ai + Si + Ti + i

(1)

Yi is an educational attainment indicator outcome of interest. The treatment indicator, BBDi , indicates whether or not BBD plausibly affects an individual’s ability or desire to graduate high school. BBDi is discussed at length in Section 4.3. Xi is a vector of individual specific variables composed of Central cityi (i lives in city center), MSAi (i lives in a MSA), Nonwhitei (i is nonwhite), and Malei (i is male). Ai picks up a cohort effect. It is a vector of indicator variables for survey ages (21, 22, 23, . . ., 29) to control for nonlinearity in HSG by age.11 Si is a vector of state specific indicator variables to control for state-specific, unobservable characteristics. Ti is a vector of year specific indicator variables, which controls for year-specific, unobservable determinants of educational attainment. i is a normally distributed random error term with mean zero. In each estimation,

7 Specification 6 of Table 7 removes years after 1989 and does not change the estimate effect of BBD on HSG. 8 The more obvious reason being to empirically test different theories of deregulation 9 See Appendix Table A2. 10 LPMs are also used in Teng Sun and Yannelis (2016). 11 I cannot differentiate between high school graduates and GED earners. If GED earning is more common, for instance, at age 24–26, then allowing for nonlinear effect of age will capture that variance in the outcome variable.

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Fig. 2. Does high school graduation predict BBD timing?

the error terms are cluster-corrected by state to address potential serial correlation. To account for heterogeneous effects of BBD on race, gender, age, etc. the sample is often split into subgroups. I estimate these subgroups separately using Eq. (1). Alternatively, I could regress the full sample with interaction terms to compare treatment effects by group. However a constrained interaction regression forces the parameter estimates to be constant across subgroups. This constraint may lead to biased parameter estimates.12 Therefore, to assist with testing for differences between subgroups, I also estimate an unconstrained interaction regression where each subgroup is allowed different intercepts for each state, year, and age identifier. Error terms of LPMs may suffer from non-normality and heteroskedasticity because of the bivariate nature of the dependent variable. To address this issue, I use the Probit estimator as a robustness check: P(Yi = 1|BBDi , Xi , Ai , Si , Ti ) = (a + ıBBDi + Xi + Ai + Si + Ti + i )(2) Probit estimates whether or not the bivariate dependent variable, Yi , equals 1 using a maximum likelihood approach. () is the cumulative distribution function of the unit-normal distribution. 4.3. Identifying the treatment group BBDi identifies individuals whose high school education was plausibly influenced by BBD. With the CPS data described in the next section, I know each survey recipient’s year of birth and state where they are currently living. I use this data to identify the treatment group. First, individuals who already reached the educational achievement of interest when BBD occurs are non-treated. For instance, if an individual graduates high school in 1980 and BBD in her/his state of residence occurred in 1981, then the BBD could not have any effect on her/his graduating high school. Even if the individual

12 For instance, for 20–29 year olds in 1977, 85.6% of white males graduated high school, 84.7% for white females. For 20–29 year olds in 1999, 83.3% of white males graduated high school, 87.1% for white females. White males are less likely to graduate, white females are more likely to graduate, but a constrained regression would force the intercepts from 1977 to 1999 to either increase or decrease for all groups.

was forward looking she/he is unlikely to pay attention to such a policy. The data does not identify the year each individual graduated high school. I instead use the fact that most individuals do not graduate high school before age 17 along with data on individuals’ ages and states of residence to sort them into treated and control groups. Unless otherwise specified, I identify individuals as treated if they were 17 or under at the time their state of residence deregulated. Therefore, BBDi is an indicator variable that identifies the treatment group, namely, BBDi = 1 if individual i was under the age of 18 when the state individual i lives in deregulated branching. Otherwise, BBDi = 0.13 To visually demonstrate the treatment criterion, Fig. 3 depicts age-year combinations in two BBD states. The rows indicate a subset of survey years. The columns indicate ages observed in the survey. The shaded cells are treated cohorts. Notice, the diagonal boundary. Shaded cells on the boundary represent 17-year-olds in the survey year. Any observations to the left/below this boundary are 17 or younger at the time their state deregulated, which is the definition of treated. Unshaded cells on the boundary represent 18-year-olds in the survey year. Any individuals to the right or above this boundary are 18 years old or older at the time their state deregulated, which is the definition of non-treated. This imprecise treatment sorting causes measurement error. One obvious challenge is derived directly from not knowing when an individual graduated high school. In this sample, 78.3% of 19-year-olds, 45.5% of 18-year-olds, and 5.4% of 17-year-olds graduated high school. Because of this imprecise sorting into “should have graduated” or “likely still in school” categories, I exclude individuals aged 18 and 19 at the time of BBD from most estimations. There may be some systematic error remaining. It is likely that I improperly place low-ability individuals in the control group, 20-year-olds or older still in high school. It is also likely that I improperly place high-ability individuals into the treated group

13 To create BBDi I use information from the CPS on the age when surveyed, AGEi , of each individual, i, the year when surveyed, YEARi , and the state of residence when surveyed, si . I create a variable called BBD yeari , which takes the value of the year of BBD of state, si . I then create another variable called age at BBDi , which takes the value of individual i’s age in the year when state, si , was deregulated: age at BBDi = (BBD yeari − (YEARi − AGEi )). Then I create the BBD treatment variable, BBDi , which, unless otherwise specified, takes a value of 1 when age at BBDi < 18, 0 otherwise.

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Fig. 3. Intent to treat strategy, two states.

because they graduated before age 17. This could bias the BBD coefficient upward. However, this applies to such a small portion of the sample that the bias is likely inconsequential.14 Another challenge for this identification strategy is that some individuals moved to another state after high school and were not influenced by BBD in their current state of residence. This unobserved migration across state lines introduces measurement error. State-to-state migration may be tied to educational attainment. Educated individuals more likely have experience away from home, e.g. going to college out of state/away from home. Also, higher educated individuals usually have greater means to move, both financial and time to search. However, most migration decisions are likely uncorrelated with BBD.15 People are unlikely to move to another state to gain access to banks with less branching regulation. Therefore, migration likely biases BBD estimates toward zero. Nonetheless, to avoid some measurement error, I restrict the sample to individuals under 30 in most models. These individuals have less time to move to other states. There may be differences in the effects of BBD on education given individuals’ age at BBD. Caucutt and Lochner (2012) demonstrated increased effects of relaxing credit constraints on younger children. To check this effect, I generate the variable: Age at BBD 12 and underi to identify individuals 12 and under at the time of BBD. Because the

14 Only 0.6% of 16-year-olds graduated high school in this sample. The effect of excluding 17-year-olds from the treatment group is addressed in robustness checks. 15 BBD is found to increase economic growth, so there may be some systematic movement toward deregulated states, especially by more educated individuals who have greater means to migrate. Estimations excluding individuals moving in the past year are included in the robustness section to investigate the effect of measurement error. Excluding known movers does not significantly change parameter estimates.

education of individuals aged 13–17 at time of BBD are plausibly affected by BBD I also include an indicator variable Age at BBD 13 to 17. 4.4. CPS data This study uses data from the CPS March Supplement from 1977 to 1999. State of residence was not available before 1977. Regardless, this time frame includes most of the variation in state BBD. Specifically, 36 states deregulated in those years. Furthermore, because of the retroactive nature of my identification, I can include observations from individuals residing in those three states where BBD occurred prior to 1977. The last intrastate BBD occurred in 1999 (Iowa). All other states deregulated by 1994. By ending in year 1999, I represent 38 states (all but Iowa) in the treated group. Limiting the dates from 1977 to 1999 narrows the set to 3.5 million observations. I exclude states deregulating before 1970 as no analogous BBD dates exist.16 This decreases the number of observations to about 2.7 million. I omit individuals surveyed before age 20 as there are many reasons why they might not have completed high school. I omit

16 Rhode Island, South Dakota, Delaware, Maryland, DC, North Carolina, South Carolina, Idaho, Nevada, Arizona, California, and Alaska deregulated bank branching before 1970. Levine and Rubinstein (2013) suggest that these states all deregulated in 1960, but the source they cite, Kroszner and Strahan (1999), only indicates that these states deregulated prior to 1970. For most studies of BBD this does not matter greatly because they are interested in how BBD effects the macroeconomy. In this paper, however, the setup of the treatment group relies heavily on the year that these states deregulated. Therefore, I omit those states and D.C. deregulating at an unknown date unless otherwise indicated.

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Table 3 Effect of BBD on high school graduation by race and gender.

Table 2 Summary statistics. Mean

sd

BBD HS Grad Some College Bachelor’s Central City MSA Male Nonwhite

0.315 0.859 0.484 0.167 0.257 0.316 0.482 0.134

0.464 0.348 0.500 0.373 0.437 0.465 0.500 0.341

Observations

386,841

Min 0 0 0 0 0 0 0 0

(1) (2) (3) HS Grad HS Grad HS Grad

Max 1 1 1 1 1 1 1 1

Notes: Data from the CPS March supplement: years 1977– 1999, ages 20–29, states deregulating after 1969. Omits survey respondents aged 18 or 19 when the state they live in deregulated. Mean is the proportion of the sample with that attribute.

individuals aged 30 and above to limit the measurement error caused by state-to-state migration. Also to avoid measurement error, I excluded individuals aged 18 or 19 at the time the state they live in deregulated. This leaves 386,841 observations in the base model. From Eq. (1), the dependent variable Yi takes on three separate binary outcome variables. HS Gradi takes the value of 1 if individual i earned at least a high school diploma or a general equivalency degree (GED), 0 otherwise.17 Some Collegei takes the value of 1 if individual i attended college, 0 otherwise. For data gathered in years 1977–1991, Bachelor si takes the value of 1 if individual i finished at least four years of college, 0 otherwise. For data gathered after 1991, Bachelor si takes the value of 1 if individual i graduated with a Bachelor’s degree, 0 otherwise. Murnane (2013) describes many factors that lower the opportunity cost of learning or moving up a grade level, e.g. parents’ income, mother’s education level, etc. Herein lies one limitation of this study; the CPS contains no data on individuals during adolescence. Therefore, I have no data on family wealth, enrollment in prekindergarten, parent education levels, etc. Rather, the CPS includes data on demographic variables, state of residence, age, and survey year. I include an indicator variable for nonwhite individuals, Nonwhitei . There are also gender differences in HSG rates. These are captured by the indicator variable, Malei . I also include geographic indicator variables Central Cityi and MSAi . Central Cityist indicates that the individual lives in a central city. MSAist indicates that individual i lives in a metropolitan area but outside of the central city. Individuals living in rural areas or individuals not answering which type of area they live in take the value of 0 for both of these indicators. Table 2 presents summary statistics of the described variables. Each mean represents the proportion of the sample population with that attribute.

BBD

0.010* (0.004)

(4) (5) HS Grad HS Grad

(6) HS Grad

0.013** −0.002 (0.005) (0.015)

0.010* −0.006 (0.004) (0.013)

0.010* (0.004) 0.003 (0.005) −0.016 (0.014) 0.001 (0.018) −0.024 (0.031) 0.113*** (0.012)

X X X X White Male 163,458

X X X X White Female 171,538

X X X X Both Both 386,841

Male × BBD Nonwhite × BBD Male × Nonwhite × BBD Male Nonwhite State indicators Year indicators Age indicators Control variables White or Nonwhite Male or female Observations

−0.009*** (0.002) −0.045*** (0.011) X X X X Both Both 386,841

X X X X Nonwhite Male 22,883

X X X X Nonwhite Female 28,962

Note: * p < 0.05, ** p < 0.01, *** p < 0.001. Standard errors clustered by state in parentheses. The dependent variable labels each specification. HS Grad = 1 if an individual graduated high school or has a GED. BBD = 1 if an individual was under age 18 when the state they live in deregulated bank branching. Specifications (1) through (5) use Eq. (1). Specification (6) is an unconstrained full interaction model that interacts nonwhite and male with factor variables for each state, year, and age. × denotes interaction terms. Each specification uses CPS March supplement data including years 1977–1999 and 39 states with mergers and acquisitions BBD after 1969. Each specification omits survey respondents aged 18 or 19 when the state they live in deregulated.

These results focus on the effect of BBD on HSG and heterogeneous effects due to differences in race, gender, and age at deregulation. To avoid constraining gender and racial groups to the same intercepts for state, year, and age fixed effects, Table 3 splits the data into four subsamples: white males, white females, nonwhite males, and nonwhite females. White males are 1.3 percentage points more likely to graduate high school after the BBD. White females are 1.0 percentage points more likely.

Although there is no evidence of significant effects for nonwhite males or nonwhite females, the differences in parameter estimates between groups is not statistically significant. Specification (6) allows each of these groups to have different state, year, and age intercepts as well as interacting Male, Nonwhite, and BBD. Results still indicate that BBD increases the likelihood of HSG by 1 percentage point, while finding no evidence of heterogeneous effects by race or gender.18 To establish the validity of the data and specifically the treatment design, Table 4 presents the effects of BBD on higher education outcomes. Teng Sun and Yannelis (2016) estimate that BBD increases college attendance by 2.6 percentage points. Using my data, I estimate around a 2 percentage point increase in college attendance for both males and females. The parameter estimate for males is significant at the 10% alpha level, females at the 5% alpha level. At the least, this consistent result fails to reject my use of retroactive treatment design and use of CPS data. The last two specifications in Table 4 analyze bachelor degree achievement of white males and white females respectively. White males see a 2.1 percentage point increase in bachelor’s degree attainment. White females enjoy a similar increase in likelihood of earning a bachelor’s degree. BBD has greater impacts on college attendance and attainment than HSG because credit more directly affects college students through student loans. Table 5 splits observations into two subsets: states with a history of unit banking and states with all other types of geographic restrictions leading up to BBD. Deregulating directly from unit banking rather than from some less restrictive policy is a more radical change to intrastate branching and may generate a greater overall

17 Cameron and Heckman (1993) find GED earners are more closely related to dropouts than to high school graduates. Unfortunately the data does not separate these education outcomes. Although this should not discredit any effects of BBD on educational outcomes, it does muddy the interpretation and any possible policy implications

18 The parameter estimates for Nonwhite and Male for specification (6) cannot be interpreted simply as every state, year, and age has a separate intercept for both Nonwhite and Male. Nonwhite is likely strongly significant because the state and year omitted in this interaction regression to avoid colliniearity were Hawaii and 1999.

5. Results

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Table 4 Data validity: college attendance and attainment.

Table 6 Comparison of treatment group by age at BBD.

(1) Some college

(2) Some college

(3) Bachelor’s

(4) Bachelor’s

BBD

0.020 (0.010)

0.022* (0.009)

0.021* (0.009)

0.020* (0.010)

State indicators Year indicators Age indicators Control variables Female or male Nonwhite or white Ages observed Observations

X X X X Male White 20–29 163,458

X X X X Female White 20-29 171,538

X X X X Male White 24–29 101,177

X X X X Female White 24–29 105,705

Note: * p < 0.05, ** p < 0.01, *** p < 0.001. Standard errors clustered by state in parentheses. The dependent variable labels each specification. Some College = 1 if the individual attended college. Bachelor s = 1 if the individual completed 4 or more years of college. BBD = 1 if an individual was under age 18 when the state they live in deregulated bank branching. Eq. (1) models each specification. Each specification uses CPS March supplement data including years 1977–1999 and 39 states with mergers and acquisitions BBD after 1969. Each specification omits survey respondents aged 18 or 19 when the state they live in deregulated.

effect on educational outcomes. The first two specifications represent models of HSG for unit banking states and non-unit banking states. Neither of these models identify BBD as a significant factor in explaining HSG. Specifications (3) and (4) model bachelor’s degree attainment in unit banking and non-unit banking states, respectively. Individuals living in non-unit banking states increase their likelihood of bachelor’s degree attainment by 2.6 percentage points. Bachelor’s degree attainment by residents of unit banking states were unaffected by BBD policy. This may seem like a puzzling result, however, the parameter estimates may not be statistically different. The estimates are relatively imprecise. Additionally, specification (6) provides parameter estimates from a model that includes an interaction term. This model fails to provide evidence to reject the notion that BBD had heterogeneous effects on unit banking and non-unit banking states. Studies by Carneiro and Heckman (2002) and Caucutt and Lochner (2012) find greater impacts on younger individuals for policies affecting investment in education. Table 6 presents a test of this claim. For younger individuals (those aged 12 and under at the time of BBD), BBD increases the likelihood of HSG by 1.3 percentage points. This is higher in magnitude than older individuals (those aged 13–17 at the time of deregulation), but not statistically different. Therefore, this does not provide strong evidence for or against the idea that BBD has a greater effect on younger individuals. Simi-

(1) HS Grad

(2) Some College

(3) Bachelor’s

Age at BBD: 12 and Under Age at BBD: 13–17

0.013* (0.005) 0.010* (0.004)

0.014 (0.015) 0.020* (0.008)

0.028* (0.012) 0.019* (0.008)

State indicators Year indicators Age indicators Ages observed R-squared Observations

X X X 20–29 0.025 386,841

X X X 20–29 0.025 386,841

X X X 24–29 0.022 238,137

Note: * p < 0.05, ** p < 0.01, *** p < 0.001. Standard errors clustered by state in parentheses. The dependent variable labels each specification. HS Grad = 1 if an individual graduated high school or has a GED. Some College = 1 if the individual attended college. Bachelor s = 1 if the individual completed 4 or more years of college. BBD = 1 if an individual was under age 18 when the state they live in deregulated bank branching. Each specification uses Eq. (1) to model the data. Each specification uses CPS March supplement data including years 1977–1999 and 39 states with mergers and acquisitions BBD after 1969. Each specification omits survey respondents aged 18 or 19 when the state they live in deregulated.

lar conclusions are drawn from models estimating the effect of BBD on college attendance and bachelor’s degree attainment. More comprehensive than Table 6, Fig. 4 depicts the dynamic impact of BBD on HSG. This figure acts in a similar way to an event study. Coefficients estimate the effect of being a certain age at the time of BBD. Those who should have graduated high school before BBD (aged 20 and over) should not be influence by the event (BBD); whereas, BBD could have some effect on those who are younger (ages 17 and under). The figure helps to describe the immediacy of the impact of BBD on HSG. One might expect less impact for those who were older at the time of deregulation for two reasons: (1) It takes time for banks to consolidate and credit it improve and (2) there is likely some inertia in terms of individuals’ educational attainment, i.e. 17-year-olds are on some trajectory when it comes to HSG and it is unlikely much anything will affect their education, but 12-year-olds or 8-year-olds are more susceptible to outside influences. The figure presents coefficient estimates and 95% confidence bands corrected for state clustering when estimating the following model.

HS Gradi = ˛ +

12 

24−j

j Di

+ 13 Di<12 +

j=0

ˇXi + Ai + Si + Ti + Si × t + i

(3)

Table 5 Comparison of unit banking vs limited branching groups.

BBD

(1) HS Grad

(2) HS Grad

(3) Bachelor’s

(4) Bachelor’s

(5) HS Grad

(6) Bachelor’s

0.015 (0.007)

0.004 (0.004)

−0.003 (0.023)

0.026** (0.008)

0.016 (0.009) −0.007 (0.022)

0.038** (0.011) 0.004 (0.013)

X X X Yes 20–29 153,407

X X X No 20–29 233,434

X X X Yes 24–29 95,085

X X X No 24–29 143,052

X X Both 20–29 386,841

X X Both 24–29 238,137

Unit banking × BBD State indicators Year indicators Age indicators Unit banking state Ages observed Observations

Note: * p < 0.05, ** p < 0.01, *** p < 0.001. Standard errors clustered by state in parentheses. The dependent variable labels each specification. HS Grad = 1 if an individual graduated high school or has a GED. Bachelor s = 1 if the individual completed 4 or more years of college. BBD = 1 if an individual was under age 18 when the state they live in deregulated bank branching. Specifications (1) through (4) use Eq. (1). Specification (5) and (6) add an interaction term, Unit Banking × BBD, to Eq. (1). This term identifies individuals from unit banking states who were under the age of 18 when their state deregulated bank branching. Each specification uses CPS March supplement data including years 1977–1999 and 39 states with mergers and acquisitions BBD after 1969. Each specification omits survey respondents aged 18 or 19 when the state they live in deregulated.

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Table 7 Robustness checks. (1) HS Grad

(2) HS Grad

(3) HS Grad

(4) HS Grad

(5) HS Grad

(6) HS Grad

(7) HS Grad

BBD

0.010** (0.004)

0.010*** (0.004)

0.007** (0.003)

0.010* (0.005)

0.011** (0.005)

0.025** (0.010)

0.011** (0.005)

State indicators Year indicators Age indicators White men State trends Treatment age Method Other Observations

X X X No No <18 LPM None 386,841

X X X No No <18 Probit None 386,841

X X X No No <17 LPM None 386,841

X X X No No <18 LPM 1977-89 253,708

X X X No No <18 LPM Same State 340,088

X X X No No <18 LPM All States 524,939

X X X Yes Yes <18 LPM None 163,458

Note: * p < 0.05, ** p < 0.01, *** p < 0.001. Standard errors clustered by state in parentheses. The dependent variable labels each specification.HS Grad = 1 if an individual graduated high school or has a GED. BBD = 1 if an individual was under age 18 when the state they live in deregulated bank branching. Specification (1) uses a linear probability model and the sample of individuals from the CPS March supplement surveyed in years 1977–1999, aged 20–29, and from the 39 states that deregulated after 1969. Specification (2) presents marginal effects from Eq. (2), a Probit model using the same observations as specification (1). Specification (3) excludes individuals aged 17, 18, and 19 the year when the state they live in deregulated. Specification (4) restricts the sample years to 1977–1989. Specification (5) excludes individuals who moved to a different state in the past year. Specification (6) uses all states and the District of Columbia and assumes that states deregulated bank branching in 1960 if their true BBD date is unknown (Levine & Rubinstein, 2013). For specification (7), state time trends are included and the observations are limited to white males.

Fig. 4. Bank branching deregulation’s effect on HS grad by age at BBD.

Eq. (3) is the same as Eq. (1) with two caveats: it is a dynamic specification and it includes state specific time trends (Si × t). 24−j Di = 1 if individual i was age 24 − j when the state she lived in deregulated, 0 otherwise. The parameter estimates are relative to the graduation likelihood of those individuals 25 years and older at the time of BBD. If properly specified, BBD should only affect the likelihood of HSG for individuals aged 17 and under. I include individuals turning 18 or 19 at the time of BBD in this model. The figure demonstrates two main points. First, BBD’s impact on HSG was fast acting and seems to be long lasting. With the exception of age 15 (slightly smaller positive estimate), all ages 17 and below at the time of BBD find similar impacts. Second, there is minimal evidence of BBD affecting those who should have already graduate high school. With the exception of 20-year-olds, those turning 17 prior to the date of BBD see no significant changes in likelihood of graduating high school. The positive estimate at 20-years-old could result from imprecise measurement of high school graduates. CPS data groups together high school graduates and GED earners. Additionally, there is a possible trend forming from ages just above

the 17-year-old threshold. This is likely caused by BBD’s impact on 18- and 19-year-olds yet to graduate from high school or earn GEDs. 6. Robustness Table 7 summarizes robustness checks where HS Gradi is the dependent variable. In Table 7, specification (1) is the baseline results for comparison. Specification (2) presents marginal effects of a Probit model. The LPM estimation technique assumes normal and homoskedastic errors, which may not hold here. The marginal effects of the Probit are nearly identical the the LPM estimates and the errors are actually larger for the LPM specification than the Probit, which suggests the LPM method with errors cluster-corrected by state provides satisfactory results. Specification (3) changes the treatment group by restricting the treatment age at the year of BBD to be 16 and under rather than 17 and under. This restriction eliminates some potentially systematic measurement error. Some individuals, for example, may have graduated high school at age 16, which, if BBD occurred in their state when they were 17, would improperly mark them as treated. However, we do not want to include those aged 17 at the time

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10 Table 8 Placebo test, false BBD dates.

BBD false date Male Nonwhite State indicators Year indicators Age indicators White or nonwhite Male or female R-squared Observations

Table A1 False BBD dates, by year.

HS Grad

HS Grad

HS Grad

HS Grad

HS Grad

State

Year

State

Year

0.008 (0.006) −0.010*** (0.002) −0.020 (0.027)

0.014 (0.008)

−0.015 (0.012)

0.010 (0.006)

−0.019 (0.014)

X X X Both Both 0.026 392,990

X X X White Male 0.032 165,900

X X X Nonwhite Male 0.033 24,310

X X X White Female 0.033 172,693

X X X Nonwhite Female 0.028 30,087

New York North Carolina Indiana Alaska Tennessee Oklahoma Missouri Massachusetts Maryland Oregon Vermont Louisiana Colorado New Hampshire New Jersey Washington DC Maine Connecticut Wisconsin Iowa Delaware Alabama Georgia Pennsylvania Michigan South Dakota

<1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 <1970 1970 1975 1976 1977 1978 1979 1980 1981 1981 1982 1983 1984 1985 1985

Nebraska Washington West Virginia Florida North Dakota South Carolina Texas Idaho Utah Rhode Island Minnesota Kentucky Arkansas California Hawaii Mississippi Ohio Illinois New Mexico Arizona Wyoming Nevada Kansas Virginia Montana

1985 1985 1986 1986 1987 1987 1987 1987 1987 1988 1988 1988 1988 1988 1988 1989 1990 1990 1990 1990 1991 1991 1993 1994 1999

Note: * p < 0.05, ** p < 0.01, *** p < 0.001. Standard errors clustered by state in parentheses. The dependent variable labels each specification. HS Grad = 1 if an individual graduated high school or has a GED. These dates use the same distribution of timing for BBD, but randomize where each state falls in that distribution. Models in this table feature false BBD dates. BBD False Dates = 1 if an individual was under age 18 during their state’s false deregulation year. Each specification uses CPS March supplement data including years 1977–1999 and 39 states with false timing of mergers and acquisitions BBD after 1969.

of deregulation in the control group, therefore, this specification omits those aged 17 when the state they lived in deregulated. The results are no different from the baseline specification. Specification (4) varies the sample years. In this case, the sample years begin in 1977 and end in 1989. The point estimates are no different when sample years are changed. This indicates that the selection of sample years of 1977–1999 does not bias the results. Additionally, the fact that there is no difference provides evidence that the CRA, which was not strictly enforced until 1989, did not confound results. One of the assumptions made when identifying the treatment was that migration from one state to another is independent of BBD, and, therefore, estimates of BBD’s effect on education are lower bounds. To test this claim, specification (5) amends the original model by restricting the sample to exclude individuals who indicated they moved to their current state of residence in the past year. A decrease in parameter estimate would suggest this assumption generates systematic bias. The point estimates and significance levels are unchanged, so there is no evidence of systematic measurement error due to recent interstate migration. Specification (6) includes observations from all states, including the 11 states and D.C. that deregulated prior to 1970. The BBD dates used for those states and D.C. are from Levine and Rubinstein (2013). This does not change sign or significance. This will mainly add observations to the treatment group because, according to Levine and Rubinstein, the 11 states and D.C. deregulated in 1960. If the likelihood of HSG increases over time and the number of treated individuals increase over time as well, one might expect a stationarity problem. Although year effects are included in all models, individual states may have their own trend in HSG rates. To account for this possibility, Specification (7) depicts estimates including state-specific linear time trends. These trends have minimal effect parameter estimates. Since it is impossible to rule out all possible confounding factors, Table 8 presents results of estimations using false BBD dates.19 Each state’s false BBD date is randomized so the distribution of false dates matches the distribution of true dates. The randomization strategy is as follows. Each state is given a random number from a uniform distribution from 0 to 1. The smallest random number is matched

19

See Appendix Table A2 for the false dates.

Note: The randomization strategy is as follows. Each state is given a random number from a uniform distribution from 0 to 1. The smallest random number is matched with the earliest BBD date. The second smallest random number is matched with the next earliest BBD date, etc.

Table A2 Does HSG predict banking legislation?

HS Grad R-squared N

(1) BBD year

(2) BBD year

−0.236 (0.320) 0.000 394,891

−1.264 (21.035) −0.028 38

Note: The dependent variable labels each specification. BBD Year is the year the state deregulated bank branching. HS Grad = 1 if the individual graduated high school or earned a GED. Parameter estimates are derived from an OLS regression of the following equation: BBD Yeari = ˛ + ˇHS Gradi + i . Specification (1) has individual level data and standard errors cluster-corrected by state in parentheses. Specification (2) collapses the data by state with standard errors in parentheses. Each specification uses CPS March supplement data including years 1977–1999 and 39 states with mergers and acquisitions BBD after1969. Each specification omits survey respondents below 20 years old, and individuals who were below age 20 or above age 30 when BBD occurred in their state.

with the earliest BBD date. The second smallest random number is matched with the next earliest BBD date, etc. Holding constant the distribution of BBD timing but randomizing the order in which states pass BBD legislation helps assess if the results are spurious. If the effect of BBD is the same when the dates are randomized, then the results may be spurious. After randomization of BBD timing, BBD has no significant effect on the likelihood of HSG. Therefore, there is no evidence of a spurious relationship. 7. Conclusion I find that BBD increased the likelihood of attaining a high school diploma or a GED. This is an important result on its own that a policy affecting credit markets has downstream effects that reach as far as secondary education. Results suggest White individuals were significantly affected while Nonwhite individuals, on average, where not significantly affected. This result is consistent with Cameron and Heckman (2001) who suggest that nonwhite individ-

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uals react less to policies regarding labor or credit markets because the underlying detriment to education developed by these groups in early childhood. Changes to affordability or benefits of education during middle/high school cannot have strong effects on these individuals because a lack of investment in early childhood reduced their academic potential and/or contributed to the development of personalities conflicting with traditional academics. This research extends recent literature by looking at the effects of BBD not only on college enrollment, but on HSG as well. The data I used limits my ability to identify the channels responsible for these effects. However, high schools do not charge tuition and therefore direct credit channels are not likely to affect HSG. This means some indirect credit channel exists. Through a labor market channel, increased credit access to firms may have redistributed wage earnings to higher skilled workers incentivizing more educational attainment. Alternatively, increased access to credit for families may have increased investment in education. There are data limitations in this study. Future research should focus on identifying the specific channels responsible for the results, as well as using longitudinal data. The ability to follow an individual’s state of residence over their lifetime would more precisely identify those affected by BBD. Additionally, knowing more about an individual’s past will reduce the influence of omitted variables such as family income and parents’ education. Even with these limitations, this study demonstrates that the structure of the financial system can have far-reaching effects on the real economy. Conflict of interest Author declares no conflict of interest. Appendix A. Appendix tables Table A1 References Aaronson, D. (2000). A note on the benefits of homeownership. Journal of Urban Economics, 47, 356–369. Amel, D. (1993). State laws affecting the geographic expansion of commercial banks. Unpublished manuscript. Board of Governors of the Federal Reserve System. Beck, T., Levine, R., & Levkov, A. (2010). Big bad banks? The winners and losers from bank deregulation in the United States. The Journal of Finance, 65, 1637–1667. Bedard, K. (2001). Human capital versus signaling models: University access and high school dropouts. Journal of Political Economy, 109, 749–775. Benmelech, E., Bergman, N., & Seru, A. (2011). Financing labor. In Working paper 17144. Black, D., McKinnish, T., & Sanders, S. (2005). Tight labor markets and the demand for education: Evidence from the coal boom and bust. Industrial and Labor Relations Review, 59, 3–16. Bostic, R. W., & Robinson, B. L. (2004). The impact of CRA agreements on community banks. Journal of Banking and Finance, 28, 3069–3095. Boustanifar, H. (2014). Finance and employment: Evidence from U.S. banking reforms. Journal of Banking and Finance, 46, 343–354. Bridgeland, J., Dilulio, J. J., Jr., & Morison, K. B. (2006). The silent epidemic: Perspectives of high school dropouts. Civic Enterprises. Cameron, S. V., & Heckman, J. J. (1993). The nonequivalence of high school equivalence. Journal of Labor Economics, 11, 1–47.

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Please cite this article in press as: Reilly, P.A. The effects of credit on high school graduation: Evidence from U.S. bank branching deregulation. The Quarterly Review of Economics and Finance (2019), https://doi.org/10.1016/j.qref.2019.05.012