A Day Late and a Dollar Short: Liquidity and Household Formation among Student Borrowers

Finance and Economics Discussion Series Divisions of Research & Statistics and Monetary Affairs Federal Reserve Board, Washington, D.C. A Day Late and a Dollar Short: Liquidity and Household Formation among Student Borrowers Sarena Goodman, Adam Isen, and Constantine Yannelis 2018-025 Please cite this paper as: Goodman, Sarena, AdamIsen, andConstantineYannelis(2018). “ADayLateandaDollar Short: Liquidity and Household Formation among Student Borrowers,” Finance and EconomicsDiscussionSeries2018-025. Washington: BoardofGovernorsoftheFederalReserve System, https://doi.org/10.17016/FEDS.2018.025. NOTE: Staff working papers in the Finance and Economics Discussion Series (FEDS) are preliminary materials circulated to stimulate discussion and critical comment. The analysis and conclusions set forth are those of the authors and do not indicate concurrence by other members of the research staff or the Board of Governors. References in publications to the Finance and Economics Discussion Series (other than acknowledgement) should be cleared with the author(s) to protect the tentative character of these papers.

A Day Late and a Dollar Short: Liquidity and Household Formation among Student Borrowers*1 Sarena Goodman Federal Reserve Board of Governors Adam Isen Office of Tax Analysis, U.S. Department of the Treasury Constantine Yannelis Department of Finance, NYU Stern School of Business April 2018 Abstract The federal government encourages human capital investment through lending and grant programs, but resources from these programs may also finance non-education activities for students whose liquidity is otherwise restricted. This paper explores this possibility, using administrative data for the universe of federal student loan borrowers linked to tax records. We examine the effects of a sharp discontinuity in program limits—generated by the timing of a student borrower’s 24th birthday—on household formation early in the lifecycle. After demonstrating that this discontinuity induces a jump in federal support, we estimate an immediate and persistent increase in homeownership, with larger effects among those most financially constrained. In the first year, borrowers with higher limits also earn less but are more likely to save; however, there are no differences in subsequent years. Finally, effects on marriage and fertility lag homeownership. Altogether, the results appear to be driven by liquidity rather than human capital or wealth effects. JEL Classification: D14, G18, H52, H8, J24 * Email: sarena.f.goodman@frb.gov, adam.isen@treasury.gov, and constantine.yannelis@stern.nyu.edu. The authors thank Markus Baldauf, Neil Bhutta, Jeffrey DeSimone, Jason Donaldson, Will Gornall, Caitlin Hesser, Caroline Hoxby, Theresa Kuchler, Song Ma, Holger Mueller, Michael Palumbo, Yochanan Shachmurove, Luke Stein and our discussant Michaela Pagel, as well as seminar and conference participants at the ASU Sonoran Winter Finance Conference, the Federal Reserve Bank of New York, NYU Stern, and the 2017 Southern Economic Association Annual Meeting for helpful comments and discussions. Any views or interpretations expressed in this paper are those of the authors and do not necessarily reflect the views of the Treasury, the Federal Reserve Board of Governors, or any other organization.

I. Introduction The federal government expends considerable resources to encourage human capital investment. Indeed, the majority of U.S. undergraduate tuition is financed by federal sources, with over $75 billion in student loans and grants disbursed in 2016 alone. Moreover, the $1.2 trillion currently owed in federally guaranteed student debt exceeds the cumulative amount outstanding from any other source of non-mortgage household debt. In standard economic models, these programs encourage investment by helping remove credit constraints from the decision to attend college and subsidizing its cost (Becker, 1962; Ben-Porath, 1967; Mankiw, 1986; Palacios, 2014). However, they may also provide liquidity to students for important non-education activities—for example, by helping homebuyers finance upfront payments required to obtain a mortgage—at a point in the lifecycle when credit is generally scarce.1 Still, the net effect of these programs on liquidity is ambiguous, as taking on student debt today might impair the availability of other credit in the future.2 Specifically, student loan balances and payment histories are used to calculate credit scores and in other aspects of credit underwriting, which could decrease spending on non-education activities, particularly if such borrowing leads to early damage to credit scores or debt overhang (Mian and Sufi, 2011; Gorea and Midrigan, 2017).3 Indeed, this possibility has dominated the public discussion of these programs, which has often attributed relatively low levels of household formation among young adults to high levels of student debt (e.g., CEA, 2016). A recent New York Times (2017) editorial noted: “Loan payments are keeping young people from getting on with life, delaying marriage and homeownership.” Ultimately, how these programs affect consumption-smoothing is an empirical question, best answered by an experiment that randomly assigns students access to additional resources and compares their early-lifecycle outcomes. In this paper, we approximate this experiment via a Department of Education (DoEd) policy rule that classifies undergraduates applying for financial 1 Unlike other types of credit, access to federal student loans does not entail credit underwriting or risk-pricing. 2 This discussion abstracts from potential effects on liquidity from investment in higher education, which we demonstrate are minimal within our setting. Note that a similar tension has been examined from the firm’s perspective, wherein relaxing firm credit constraints can spur investment but high resulting levels of debt can reduce investment later on through a debt overhang channel (Albuquerque and Hopenhayn, 2004; Myers, 1977; Whited, 1992). 3 These effects may be amplified if potential recipients are debt averse (Caetano, Palacios, and Patrinos, 2011), myopic (Benartzi and Thaler, 1995), or inattentive (Pagel, forthcoming). Note that, for borrowers who meet their student loan obligations, credit availability could be enhanced or expanded via the establishment of a strong credit record, in which case spending on non-education activities may increase. 2

aid as either financially dependent or financially independent, a key determinant of the amount of federal support that they can receive (i.e., their federal loan and grant “limit”), based on the timing of their 24th birthday.4 Specifically, those who are at least 24 years old in the calendar year they enroll are considered independent; thus, students whose 24th birthdays fall just before January 1 generally face a higher limit than their classmates whose birthdays fall immediately after that date. A substantial fraction of college students are likely affected by this rule.5 The analysis links administrative federal student loan, grant, and tax records and uses a regression discontinuity design (RDD) to credibly estimate the effects of access to additional resources through these programs on household formation. Exploiting the sharp cutoff in limits this rule generates over student borrowers’ birthdates to approximate random assignment, we primarily examine homeownership—but also earnings, savings, marriage, and fertility—in the year of the discontinuity and up to five years later.6 Several specific features of our design help isolate the direct effects of resources from those that could stem from spending on human capital, which we confirm with an extensive analysis of potential mechanisms.7 We first estimate that, in the year of discontinuity, borrowers with higher limits receive about 40 percent more federal loans and grants than their peers, which is driven by increased borrowing. We then find that the discontinuity induces an immediate 0.5 percentage point (p.p.) jump in homeownership, evidence that these programs help student borrowers finance important noneducation spending.8 This effect is robust, with no evidence of effects among same-aged placebo 4 The use of the term “limit” throughout this paper is related to but differs from the statutory loan limits published by the DoEd. Our use accords with the credit market definition of the term and refers to the maximum cumulative loan and grant amount that a given student may receive. Within our experiment, this limit can vary with the full set of particular statutory limits faced as well as a student’s calculated financial need. 5 Completing college within four years of high school graduation has become much less commonplace over time, while borrowing for college has become more so. In 2011–2012, 44 percent of undergraduates were at least 24 years old and 59 percent were receiving federal support. These points are discussed further in Section 2. 6 The identifying assumption generates testable implications, which we are able to validate. Namely, the density of borrowers with respect to the assignment variable is continuous in the vicinity of the discontinuity, and predetermined variables evolve smoothly in this region as well. 7 Namely, the design exploits marginal changes in limits within a sample comprised of borrowers who had previously taken out loans, who had already applied for financial assistance for the upcoming year, and who attend public and private nonprofit institutions (among whom there is no evidence of enrollment effects). 8 Purchasing a home generally entails upfront payments, usually to meet a down payment requirement (the percentage of the home that must be paid at settlement) and closing costs (the costs associated with processing the paperwork to buy a house). These costs may represent an impediment for first-time homebuyers, who tend to earn less, purchase less expensive houses, and finance their home purchases with Federal Housing Administration (FHA) loans, which offer lower upfront costs at the expense of higher downstream costs (NAR, 2016; FHFA, 2013). (The minimum down payment for an FHA loan is 3.5 percent of the purchase price, far lower than the 20 percent usually recommended for 3

populations that should not be affected by the policy rule. It also persists through the medium run, and is later echoed by an increase in family formation as measured by marriage and fertility, consistent with a net positive effect on liquidity over this horizon. In an analysis of mechanisms, we examine labor market and savings responses, as well as potential sources of heterogeneity, and demonstrate that increased liquidity best explains our results. Consistent with our design, we first find very little evidence that the marginal dollar in our setting is financing or improving human capital. While borrowers have marginally lower earnings in the year of the discontinuity (consistent with additional financial resources helping students meet expenses or bolster discretionary spending), estimates in all subsequent years are indistinguishable from zero and can rule out more than modest effects. In addition, we find no effect on enrollment intensity or attainment, even in the short run. Furthermore, even though they earn less, borrowers with higher limits are 2.5 percentage points more likely to save (i.e., have a savings or investment account) in the year of the discontinuity, with no discernible differences in subsequent years, consistent with an immediate increase in resources that are not allocated toward education but are otherwise quickly spent down (reflective of financial constraints). Second, we show that the results appear to be driven by liquidity (as opposed to increased wealth), as effects are concentrated among borrowers who are particularly financially constrained and who see little or no change in grants.9 In addition, the effects are largest, and still concentrated among these borrowers, after access to other forms of credit tightened during the Great Recession. To our knowledge, there has been no work exploring whether young adults extract liquidity from the federal student loan and grant programs. Thus, our core finding that higher program limits facilitate spending on important non-education activities is a novel result and suggests that these programs represent a crucial credit instrument for this demographic. While, to demonstrate this function, our study isolates a setting in which student loans and grants are not financing education, the liquidity benefits of these programs may also extend to contexts in which they spur education investment (provided there is still some crowd out of education spending). In addition, the a conventional home mortgage loan.) According to Navient (2015), 21 percent of young adults without a mortgage list not having funds for a down payment as the rationale. 9 Namely, the effects are driven by borrowers with an expected family contribution (EFC) of 0 in the prior year, who tend to both be more financially constrained (as their families have relatively low income and assets) and experience smaller changes in subsidy. Increases in subsidy are exclusively driven by decreases in EFC, but zero-EFC borrowers are already at the lower bound; thus, the increase in federal support for this group is driven by increased borrowing stemming from the higher borrowing limit. 4

formulation of the analysis sample generates a new finding with respect to enrollment, specifically that marginal loan and grant dollars appear to only finance education at for-profit institutions, at least among individuals on the cusp of turning 24 years old.10 The results add to several literatures. First, a body of work examines the determinants of household formation, both generally (e.g., Paciorek, 2016) and among young adults (Bhutta, 2015; Martins and Villanueva, 2009). The most related studies demonstrate the importance of liquidity and the availability of credit (Campbell and Cocco, 2003; DeFusco, Johnson, and Mondragon, 2017; Gorea and Midrigan, 2017; Mian and Sufi, 2011, 2015) and indicate that down payment constraints bind for many young households (Engelhardt, 1996; Fuster and Zafar, 2016; Berger, Turner, and Zwick, 2016). Other work finds that consumer debt, and sometimes specifically student loan debt, reduces formation; however, these studies generally attempt to compare individuals who are similar on all dimensions except for their liabilities and thus focus only on the potential negative effects of debt (Bleemer et al., 2014 and 2017; Mezza et al., 2016; Dettling and Hsu, 2017; Chiteji, 2007).11 A second, related literature, motivated by the canonical permanent-income hypothesis, evaluates whether liquidity motivates consumer behaviors more generally. Within this literature, our setting is most similar to work that has examined consumer response to changes in credit availability (e.g., Deaton, 1991; Carroll, 1992; Ludvigson, 1999; Mian, Rao, and Sufi, 2013; Mondragon, 2017; Baker, forthcoming; Souleles, 1999; Gross and Souleles, 2002; Melzer, 2011). In particular, Gross and Souleles (2002) estimate that spending is quite sensitive to credit card limits and interest rates, across the distribution but particularly among those already close to their limits, consistent with binding liquidity constraints. Finally, our results contribute to work examining federal student loan and grant programs. They reveal that these programs enable spending on important non-education activities and increase household formation. However, they also indicate that, with respect to human capital, the 10 Specifically, we leverage the full breadth of the tax data and test for potential extensive margin responses, which could introduce bias into the estimates and confound their interpretation as distinct from human capital effects. We discover clear enrollment effects at for-profits but negligible effects elsewhere, consistent with the for-profit sector being uniquely adept at identifying and enrolling students who are eligible for more federal financing. 11 In particular, these studies do not isolate changes in cash on hand. Mezza et al. (2016) and Bleemer et al. (2017) find negative effects of student debt instrumented by increases in tuition. Dettling and Hsu (2017) and Bleemer et al. (2014) find evidence that less advantageous credit positions affect the probability of living with parents (though Chiteji (2007) does not). We do not view our findings as being necessarily inconsistent with these studies, but rather as implying that any negative effects of debt increases within our setting are dominated by alternative channels (e.g., liquidity effects). 5

marginal dollar has a low return on investment within our context: It only raises attendance within a notoriously low-return sector, and, within the much larger public and private nonprofit sectors, it does not increase earnings. Avery and Turner (2012) and Looney and Yannelis (2015) describe pertinent aspects of the student loan market. Lochner and Monge-Naranjo (2016) and Palacios (2014) study the theoretical framework for student borrowing and human capital investment. Most of the empirical work investigates the determinants of take-up of these programs and their effects on human capital accumulation (e.g., Dynarski, 2003; Stinebrickner and Stinebrickner, 2008; Lochner and Monge-Naranjo, 2011; Bettinger, Long, Oreopoulos, and Sanbonmatsu, 2012; Dynarski and Scott-Clayton, 2013; Marx and Turner, 2015; Denning, 2017; Angrist et al., 2017; Denning, Marx, and Turner, 2017; Solis, 2017). Otherwise, they examine the interplay between such programs and other forms of education financing (e.g., Lucca, Nadauld, and Shen, 2017; Amromin, Eberly, and Mondragon, 2016; Turner, 2017; Cox, 2017). The rest of this paper is organized as follows. Section II describes the policy environment and data sources. Section III discusses the identification strategy, sample restrictions, and balance tests. Section IV presents the main estimates and examines robustness. Section V describes and evaluates mechanisms. Section VI examines family formation. Section VII concludes. II. Research Design A. Institutional Background The majority of U.S. undergraduate tuition is financed by federal sources through programs established under Title IV of the Higher Education Act of 1965. The largest of these programs, and the focus of our study, are the two major student lending programs, the Federal Direct Loan (DL) Program and the (now-defunct) Federal Family Education Loan (FFEL) Program, as well as the Pell Grant Program. The reach of these programs has expanded considerably over the past several decades, driven primarily by rising college enrollments and attendance costs: In the 2015–2016 academic year, more than 7.1 million undergraduates received a loan and 7.6 million received a grant, compared with 4.3 million and 3.9 million undergraduates, respectively, in the 2000–2001 academic year. In addition, as reliance on these programs has grown, student debt has become an increasingly important component of household balance sheets: According to credit bureau data, there were 43 million individuals with student debt in 2014 (almost double the amount from a 6

decade prior), with an average balance of about $27,000.12 Approximately 40 percent of households headed by an individual under the age of 35 years old have a student loan (Navient, 2015). In this section, we describe aspects of these programs relevant for our study, highlighting the dimensions along which financial dependency status, per the DoEd definition, can influence the loan and grant amounts for which a student is eligible. To receive financial assistance through the Title IV programs, students must first be deemed eligible according to a standardized application, the Free Application for Federal Student Aid (FAFSA). The FAFSA collects the demographic, asset, and income information of students and their households pertaining to the calendar year prior to enrollment, much of which is available on tax forms.13 These data are entered into a complex nonlinear formula to compute a student’s EFC, the dollar amount that the federal government determines a family can contribute to college expenses in the coming year.14 The inputs and weights of this formula vary with a student’s dependency status; for example, parents’ assets and income are key elements of a dependent student’s EFC calculation and are not included in an independent student’s calculation, which, as a result, often yields a lower EFC. The EFC is subtracted from the cost of attendance (COA) of the college to determine the student's “financial need.” Students learn of the types and amounts of federal assistance for which they are eligible via an award letter from the college in which they are enrolled or planning to attend. Undergraduate loans through the DL and FFEL programs are borrowed funds that must be repaid with interest. The “Stafford Loan,” the main brand of such loans, features standardized terms, a congressionally set interest rate, and a statutory limit.15 Besides these features, compared 12 While a private market for student lending exists, the size of this market has always been considerably dwarfed by the federal lending programs—even more so as the credit market began to experience increased regulatory scrutiny. According to The College Board’s Trends in Student Aid report, in the 2011–2012 academic year nearly $80 billion was disbursed in student loans, and 92 percent of that disbursement was through federal programs. 13 Students generally wait until after the prior year’s tax returns are filed to complete the FAFSA. A fraction of FAFSA applications are audited by the DoEd, and the IRS verifies income. 14 While the majority of financial aid is distributed through federal programs (College Board, 2015), the EFC is often a factor in institutional and state aid determinations as well. Regression analyses using the restricted-access 2007– 2008 and 2011–2012 NPSAS reveal a precisely estimated negative relationship between EFC and state and institutional aid: -0.016 (.002). Interactions between the policy rule we leverage in this study and access to or receipt of other forms of financial aid could violate the exclusion restriction necessary to generate 2SLS estimates of the effects of federal student loans and grants on household formation. 15 Prior to 2010, when the FFEL program was eliminated by the Health Care and Education Reconciliation Act of 2010, both the DL and FFEL programs issued Stafford Loans. Stafford Loans are backed by the government, though DLs are financed through direct federal funds and FFELs through private capital. Either program could disburse both subsidized and unsubsidized Stafford Loans, subject to the same loan limits. 7

with other forms of credit, including educational loans made through the private sector, Stafford Loans can be made to any student who meets the basic eligibility criteria for federal financial aid programs, even those with thin or adverse credit histories. Stafford Loans come in two varieties: subsidized loans, which are need-based, and unsubsidized loans, which are not. For subsidized loans, interest that accrues early in the life of the loan (e.g., while borrowers are in school) is paid by the government.16 For both loan types, borrowing is subject to statutory annual limits: The limit for subsidized loans varies with academic level while the cumulative (i.e., subsidized and unsubsidized) limit varies with both academic level and dependency status. Limits over time are shown in Appendix Table A.1. As a general rule, all else equal, independent students may borrow more than dependent students. For example, in 2016–2017, when the interest rate on new Stafford Loans was 3.76 percent, dependent undergraduates in their third-year and above could borrow up to $7,500, while independent undergraduates at the same level could borrow up to $12,500, with no more than $5,500 in subsidized loans in either instance. Pell Grants are need-based grants to low- and middle-income undergraduate students. The size of the award is a function of a student’s financial need, the statutory limit for the maximum grant that can be awarded in a given year (e.g., $5,815 for 2016–2017), and the student’s anticipated enrollment intensity in the coming year. As with loans, Pell Grant–eligible student can apply the funds to school costs, receive the grant directly, or combine these methods. In sum, dependency status influences the level of loans and grants that a student can receive in a given year along several dimensions. Most directly, it determines the total dollar amount a student may borrow through the Stafford Loan programs.17 In addition, for a subset of students, it affects the formula that determines financial need and thus can alter the maximum amount of Pell 16 Interest rates are set by Congress for both loan types, such that most student borrowers receive a more favorable rate than the market would generally offer them. 17 While not the focus of this study, Parent PLUS loans are another brand of Title IV undergraduate-level loans that may be influenced by dependency status as, by definition, they are only available to dependent students. The annual volume of lending through the Parent PLUS loan program is about one-fifth that of the Stafford Loan program, with the key differences being that, for Parent PLUS loans, a student’s parent, rather than the student, commits to repaying the loan, the parent’s credit history is taken into account in determining eligibility, the interest rate is generally several percentage points higher, and parents can borrow up to the cost of attendance (which includes living expenses) less other financial aid. Within our analysis, the estimated decrease in PLUS loans among financially independent students represents only a portion of the increase in Stafford Loans, which we interpret as a shift in who bears the burden of a debt load that would have been acquired in either state of the world. In a similar fashion, due to almost identical rules in the tax code for claiming dependents (children can be claimed as dependents if they are under 24 and enrolled in college), there is also a transfer (and possible overall reduction) of tax benefits from parents to the student due to education and other tax preferences. 8

Grant and subsidized loans for which a student is eligible. Key for our design, undergraduate students who are at least 24 years old by the end of the calendar year they enroll are automatically considered financially independent.18 This policy rule creates a situation where students with very similar age profiles, who are born a few days apart, face very sharp differences in limits. Many students are potentially exposed to this policy rule.19 In a nationally representative DoEd survey of undergraduates in 2011–2012, 59 percent were receiving federal support and 44 percent were at least 24 years old. While the latter figure may seem high within a framework that assumes undergraduates complete their degree within four years of graduating high school, such a framework is not today’s norm: According to a separate DoEd survey of students who completed a B.A. in 2007–2008, the average time to degree was six years, and nearly 40 percent of recipients took more than five years. Also within the 2011–2012 survey, 23 percent of undergraduates and 55 percent of Stafford Loan recipients borrowed at their “individual limit.” This rate is reflective of behaviors within both financial dependency groups. Specifically, among financially dependent undergraduates, 24 percent borrowed at this limit (pointing to a binding constraint, which is then relaxed by the policy variation), and among financially independent undergraduates, 21 percent did. B. Data The analysis relies on a linkage between two administrative data sources: 1) the DoEd’s National Student Loan Data System (NSLDS) and 2) individual tax records filed with the Internal Revenue Service (IRS). The reliance on administrative data minimizes concerns regarding sample selection, attrition, and measurement error. The NSLDS is a large administrative database containing the enrollment and federal student loan and grant records for the full universe of individuals that receive financial assistance through the Title IV programs. It includes student loan records from 1969 to the present, with newly originated loans reported to the system within 30 days of disbursement, and assembles data from a variety of sources, including schools, guaranty agencies, loan servicers, and DoEd programs, to 18 Other relevant factors include the student’s active duty or veteran status and family circumstances concerning marriage, own dependents, emancipation, homelessness, and foster care. 19 For statistics related to borrowing behaviors at the individual limit, see the NCES Stats in Brief.. For statistics related to age ranges and federal support of undergraduates, see the NCES Digest of Education Statistics. For statistics related to time to degree, see the NCES Web Tables, table 2.8. 9

assess loan eligibility, track disbursement of loans, and monitor the repayment status of loans. For this study, we use detailed information pertaining to loans (e.g., balances, counts, subsidized/unsubsidized/Parent PLUS), financial aid applications (e.g., family income, date of birth), Pell Grant disbursements, and enrollment. The IRS data cover the full universe of individuals with tax records from 1999 and 2015 and describe information from their tax returns as well as from mandatory third-party reporting on their behalf by employers and institutions, including schools. To conduct our analysis, we use mortgage data from 1098 information returns (filed by lending institutions), earnings data from W-2 information returns (filed by employers), enrollment data from 1098-T information returns (filed by colleges), and interest and dividend income data—to measure savings—from 1099 information returns (filed by financial institutions).20 We also separately observe marital status from filing form 1040 (filed by individuals and households) and births of new children from Social Security Card applications. Finally, we use outcomes measured in prior years and available demographics (citizenship, gender, family income) in the IRS data to test for balance in the research design. Many of these variables are reported on tax forms, though gender and citizenship come from social security records. III. Empirical Strategy A. Estimating Equation There can be a large difference in the amount of loans and grants for which borrowers are eligible based on whether they are deemed financially dependent or independent by the DoEd guidelines. This difference implies a sharp discontinuity in limits among those on the cusp of turning 24 years old whose birthday falls on either side of January 1. Under assumptions described below, we can use this setting to identify the causal effect of higher limits on the federal resources borrowers receive and on household formation. We estimate the following regression discontinuity 20 Our main outcome is measured by Form 1098, which is a required filing for any lender that receives at least $600 of mortgage interest during a calendar year, and, according to the form instructions, only one “payer of record” may be designated. Thus, within our design, “homeownership” is defined based on whether the individual or spouse has been designated on such a form. Note that neither the balance test nor the analysis of family formation is consistent with possible marriage effects driving effects on homeownership. Other information returns have similar reporting requirements; for example, W-2s are mandatory to file if labor earnings are at least $600, and 1099-INT and 1099- DIV are mandatory for interest or dividend income of at least $10 (though a significant number are filed that report less income). 10

design (RDD) equation: (cid:2870) (cid:1851) (cid:3404) (cid:2010) (cid:3397)(cid:2010) 1(cid:4670)(cid:1830) (cid:3408) (cid:1830)(cid:3365)(cid:4671) (cid:3397)(cid:3533)(cid:3419)(cid:2012) (cid:1830) (cid:3037) (cid:3397)(cid:2030) 1(cid:4670)(cid:1830) (cid:3408) (cid:1830)(cid:3365)(cid:4671) ∗(cid:1830) (cid:3037) (cid:3423)(cid:3397)(cid:2011) (cid:3397) (cid:2013) (cid:3036)(cid:3047) (cid:2868) (cid:2869) (cid:3036)(cid:3047) (cid:3037) (cid:3036)(cid:3047) (cid:3037) (cid:3036)(cid:3047) (cid:3036)(cid:3047) (cid:3047) (cid:3036)(cid:3047) (cid:3037)(cid:2880)(cid:2869) where (cid:1861) and (cid:1872) index borrowers and cohorts, respectively. (cid:1851) is an outcome over a particular horizon (cid:3036)(cid:3047) (e.g., total grants and loans in the year of the discontinuity, homeownership in the year of the discontinuity, homeownership two years after the discontinuity).21 1(cid:4670)(cid:1830) (cid:3408) (cid:1830)(cid:3365)(cid:4671) is an indicator for whether the borrower is 24 years old as of December 31 and thus potentially eligible for higher limits. (cid:1830) is a borrower’s age in days, centered to equal 0 for those with a January 1 birthday, included as a quadratic polynomial that is fully interacted with 1(cid:4670)(cid:1830) (cid:3408) (cid:1830)(cid:3365)(cid:4671). In our main specification, we follow Gelman and Imbens (2014) and use a second-order polynomial. In the appendix, we include only a first-order polynomial and show that our results are not sensitive to this choice. The term (cid:2011) is a cohort effect, and standard errors are clustered on the assignment (cid:3047) variable, (cid:1830). (cid:2010) identifies causal effects if the RDD continuity assumption is met—namely, the conditional (cid:2869) distribution of unobserved determinants of borrower outcomes is continuous in the vicinity of the January 1 threshold. If so, borrowers are as good as randomly assigned to their limits, and we may attribute any differences in outcomes across the threshold to the discontinuous increase in limits generated by the policy rule. While the continuity assumption is not directly testable, for it to hold, all other factors, including those that could be determinants of our outcomes, must be smooth in the vicinity of the threshold, and there should be no evidence of borrower sorting. More formally, the assumption generates two testable implications—(1) the conditional distribution of borrowers’ predetermined characteristics should be continuous through January 1, and (2) the conditional density of borrowers should be continuous as well—which we use to inform our sample restrictions and help validate our design in the next section. B. Sample Construction and an Exploration of Extensive Margin Responses 21 Technically, because the discontinuity in loans and grants occurs over an academic year but our outcomes are measured on the calendar year level, t indexes cohorts by calendar year, whereby t=0 refers to the calendar year that coincides with the ending of the academic year relevant for the policy rule. Outcomes measured “in the year of the discontinuity” refer to t=0 outcomes. Note that as t=-1 outcomes could partially reflect the policy variation (during the fall semester), when we examine prior characteristics, we consider those observed in t=-2. 11

The analysis examines federal student loan borrowers who will turn 24 years old within the academic year who had taken student loans in a prior academic year.22 The sample includes individuals who meet these criteria between the 1998–1999 and 2012–2013 academic years (inclusive). The rationale for this focus is threefold. One, in general, RDD relies on a comparison between individuals who were exposed to the policy rule and those who were nearly exposed. In theory, for our setting, anyone on the cusp of turning 24 years old would qualify, but, as many people in that age range do not attend college, centering our analyses around those who do will increase the chance that we have ample statistical power to detect effects. Two, students who borrowed in prior years are less likely to be induced into borrowing by the policy rule, which helps us meet key identification criteria.23 This issue is described more fully below and examined thoroughly. Three, this focus allows us to have more complete records—spanning the union of the tax and student loan data—for our entire sample. Next, we consider whether we need additional restrictions to be able to analyze a sample free of sample selection bias. The primary concern is that the higher limits available to independent students could affect college enrollment decisions or, because we focus on borrowers, the take-up of student loans. Though responses along either of these margins are interesting and may have important policy implications, they could result in additional mass on one side of the discontinuity, a violation of the RDD identification requirement that the distribution be smooth over the range of study. In addition, a sample free of enrollment effects will help isolate the liquidity effects of student loans and grants from potential effects on human capital. We consider extensive margin effects by sector. To do so, we first leverage the wider sample that can be formed from the tax data and examine the smoothness of the distribution of individuals in college—i.e., whether the policy rule appears to discontinuously influence attendance behavior—with both visual and regression-based evidence. Figure 1 shows enrollment effects by sector and indicates that any extensive margin effects appear to be concentrated within the for- 22 The sample excludes first-year students. We also drop any borrowers deemed financially independent in prior years to further increase the share of our sample influenced by the discontinuity, but without introducing selection bias. We later demonstrate in a placebo analysis that borrowers considered independent in a prior year exhibit no statistical difference in outcomes through the threshold. 23 We find that those who did not borrow in prior years are indeed more likely to borrow in response to higher limits, but there is no evidence that they are more likely to enroll in college. 12

profit sector.24 Table A.2 confirms the visual evidence in a regression framework matching our main specification. While this finding is of independent interest, to satisfy the continuity assumption and for ease of interpretation, we remove borrowers attending for-profit colleges from our sample. We make two final sample restrictions for the main analysis, both of which we perturb in our robustness section to demonstrate that they do not materially affect the results. First, following Yannelis (2016) and Denning (2017), we drop individuals born within three days of January 1. Dropping this “donut hole” avoids concerns about the retiming of birth due to tax incentives (Dickert-Conlin and Chandra, 1999; Turner, 2017).25 Second, to ensure that the group formed from borrowers eligible for higher limits is comparable to the one from those who are not, we use the Calonico, Cattaneo, and Titiunik (2014) method to select the optimal bandwidth of birthdates, which leads us to restrict the main sample to those born within 50 days of January 1. Figure 2 plots the density of borrowers for the final sample, subject to all of the above restrictions, which, together with the results of a McCrary (2008) test, indicate that the distribution is smooth in the vicinity of the threshold.26 C. Sample Description and Balance Table 1 presents summary statistics, and Appendix Table A.3 describes the main analysis variables. The average student borrower in our sample borrows about $6,500 in Stafford Loans in the year of the discontinuity, of which a small majority is in need-based loans. The average Pell Grant is substantially lower, about $1,800, reflecting a combination of the more restrictive 24 These differences may imply that for-profit institutions are better at targeting and enrolling students who can receive more federal financing or perhaps that students attending for-profits are relatively more aware of or sensitive to their limits. This finding, discussed in more depth in the conclusion, is worthy of further study, as recent work has shown that despite relatively high costs, the labor market return from a for-profit education is at or below that from peer institutions (Deming, Katz, and Goldin, 2012; Deming et al., 2016; Cellini and Turner, 2016) and that for-profit institutions better capture federal aid (Cellini and Goldin, 2014; Lucca, Nadauld, and Shen, 2017; Turner, 2017). Otherwise, the evidence is consistent with studies that have generally not found effects of marginal increases in federal grant and loan programs on enrollment (Kane, 1995; Seftor and Turner, 2002; Turner, 2017; Marx and Turner, 2015). Note that while Bettinger et al. (2012) found large enrollment effects of filling out the FAFSA, all students in the sample have already filled out the FAFSA and thus were ostensibly planning to enroll. 25 A related potential concern is that kindergarten entrance cutoffs are correlated with January 1; however, the vast majority of state cutoffs are in September and October (NCES). Further, we show in same-aged placebo samples there is no effect on our outcomes of interest. 26 Figure A.1 shows that the density remains smooth for more refined borrower bins as well. 13

eligibility criteria and a lower annual limit. Finally, over 60 percent of students are in their fourth or fifth academic year. The homeownership rate in the year of the discontinuity is 5 percent, and it doubles by the next year. These rates are broadly consistent with overall formation rates estimated over a similar period—namely, between 1999 and 2011, Bhutta (2015) finds that, on average, 6 percent of 20-25 year olds became homeowners within the next two years. It then increases considerably as the sample ages, reaching 34 percent five years later. The fraction of married individuals quadruples over the same window, from 11 percent to 40 percent, and the fertility rate more than sextuples. Still, a majority of individuals do not have children at the end of the study horizon. The saving rate, on the other hand, inches up steadily over the horizon: In the year of discontinuity, just over 20 percent of the sample saves compared with just over 25 percent five years later. Earnings jump after the year of the discontinuity and continue to increase as the sample ages, which likely reflects declining enrollment. Note that this pattern is, more generally, consistent with lifecycle earnings profiles. Labor force participation rates, defined as the presence of earnings, essentially do not change with age: Around 90 percent of borrowers have some earnings in each period. The RDD identification assumption implies that borrowers’ predetermined characteristics will be similar across the threshold. The intuition is that, if the policy cutoff approximates random assignment, then borrowers should appear to be similar on each side. Table 2 presents the results of a formal balance test of prior observations of the main lifecycle outcomes we examine and academic outcomes, as well as demographics, using the main RDD estimating equation. In general, estimates are not statistically significant, lending credence to the validity of our design. Further, consistent with the analysis in the prior section, Table 2 presents estimated effects on postsecondary institution type (e.g., four-year versus two-year, public versus private) and borrower academic level and finds no evidence of sorting on these dimensions. Figure A.2 plots corresponding visual evidence that prior observations of outcomes are continuous in the vicinity of the threshold. IV. Main Results A. Effects on Federal Student Loans and Grants Figure 3 depicts receipt of federal student loans and grants within the academic year of the discontinuity, cumulatively and by category, around the dependency threshold. The figures are 14

constructed similarly to those prior, with means of each outcome plotted in 20-day birthdate bins. But, in stark comparison with the earlier figures, there are clear breaks around the threshold in each figure, visual evidence that the policy rule substantially influences the federal support that borrowers receive.27 Table 3 confirms this visual evidence in the regression framework, whereby each cell contains an estimate of (cid:2010) with the outcome denoted by the column header.28 Specifically, the first column (cid:2869) indicates that those who are 24 years old within the calendar year, on average, borrow about $1,900 dollars in additional loans. Columns (2) and (3) indicate that the bulk of the increase is in needbased loans, which jump nearly twice as much as non-need-based loans. Column (4) indicates that the policy rule also leads to an additional $1,300 in Pell Grants, on average. Finally, column (5) showcases that the combined effect on loans and grants is quite substantial—nearly $3,300— implying about a 40 percent jump relative to borrowers born after the cutoff within our data. B. Effects on Homeownership by Year Figure 4 presents the main analysis graphically, plotting homeownership rates in each year up to 5 years after the discontinuity. Each graph reveals a sharp drop in homeownership to the right of the discontinuity across the full horizon, signifying an increase in homeownership among borrowers with higher limits. Contrary to much of the public discourse, increased access to loan dollars appears to be commensurate with more homeownership. Table 4 presents the corresponding regression results. In general, the estimates indicate that homeownership is significantly higher among those with higher limits. They imply an immediate effect of about 0.5 p.p. in the year of the discontinuity and a more than 1 p.p. effect over the medium run.29 C. Robustness and Placebo Estimates 27 Table A.4 presents estimates incorporating potential effects on Parent PLUS borrowing. The results indicate that the policy rule induces an about $325 decrease in such loans, less than 20 percent of the increase in Stafford Loan borrowing, suggestive of partial substitution between these loan types when terms change. As these loans require a commitment from a student’s parent, the policy rule not only induces an increase in overall borrowing but also a slight shift in payment responsibility from parents to their children. 28 Figure A.3 shows that these estimates are not sensitive to specifications with linear splines. 29 By five years after the discontinuity, we have lost nearly 25 percent of the sample, and the coefficient is no longer statistically significant; nonetheless, the magnitude remains in line with the other estimates. 15

Figure 5 shows that the estimated effects on homeownership are broadly robust to varying the bandwidth between 20 and 80 days around the threshold. It plots point estimates, as well as a 95 percent confidence interval, for each specified bandwidth. Estimates are quite stable throughout. Tables A.5 and A.6 show that the results are robust to adding borrowers within the “donut hole” back to the sample and that the point estimates are stable to using a linear spline rather than a quadratic one (though some precision is lost for later years as we lose sample). Further, Figure A.4 highlights that the point estimates using a linear spline are not particularly sensitive to bandwidth, with the estimated optimal bandwidth pointing to a smaller bandwidth than with the quadratic specification (namely, approximately 40 days, as is presented in Table A.6). Table 5 presents results of placebo analyses of same-aged groups whose behaviors should not be influenced by the policy to confirm that the effects are driven by the policy rule versus other elements of the design. The first row examines individuals who borrowed in other years but not the year of the discontinuity and thus were unaffected by the policy rule. In no column is the result statistically significant, and the zeroes are precisely estimated. The second row examines borrowers who were financially independent prior to the year of the discontinuity and who therefore should not experience differential changes in their limits that coincide with the policy rule. Again, the analysis generates no evidence of any effect. Figure A.5 demonstrates that the results pass a relabeling permutation test, a different placebo analysis that re-estimates effects varying the threshold. Estimates using thresholds far away from the true threshold are generally not statistically significant, while those using thresholds nearer to the true threshold generally are and constitute the largest magnitudes. The results indicate that the main findings are not driven by nonlinearities in the density of the assignment variable. V. Mechanisms There are several, non-mutually exclusive channels through which limit increases could lead to an increase in homeownership. First, they may influence investment in human capital, which could be complementary to household formation or generate differences in labor outcomes that influence housing choices. Second, there may be direct wealth effects, whereby additional subsidies induce increased spending on housing. Finally, they may help alleviate liquidity constraints, either directly by making more dollars available immediately or indirectly by helping 16

borrowers establish a credit history and raise their credit scores, which would increase future access to other types of credit. In this section, we probe these mechanisms and show that human capital and wealth effects do not drive our results, instead finding empirical support for a liquidity channel.30 The analysis begins with an examination of outcomes that speak to these mechanisms and demonstrates, both empirically and logically, that human capital effects are negligible. The remainder decomposes the sample to investigate heterogeneity and shows that results are concentrated among groups for whom the limit increase primarily represents a shock to their liquidity rather than wealth. A. Human Capital Effects To explore human capital effects, we primarily examine earnings and labor force participation. The first two columns of Figure 6 present these outcomes within three representative years, the year of the discontinuity, three years later, and five years later.31 There appears to be an immediate jump in earnings at the threshold, implying that borrowers eligible for higher limits earn less in the year of the discontinuity. In subsequent years, earnings and labor force participation appear to evolve smoothly. Table 6 presents the regression estimates for these outcomes. In the year of the discontinuity, there is a marginally significant earnings decrease of about $240 but a precise zero effect on participation. Note that the earnings decrease is consistent with both a reduction in labor supply and an easing of liquidity constraints (though the earnings reduction is an order of magnitude smaller than the increase in loans and grants). More importantly, higher limits do not appear to translate into additional human capital, as there are no discernible effects on earnings or participation in subsequent years. Indeed, the estimates are precise enough to rule out a 0.4 30 An information channel that stems from experience managing debt could also help generate our results. Such experience may increase familiarity with repayment options and the credit market more generally, which could influence a borrower’s likelihood of taking out a home mortgage later in life. Related work has found large effects of information on the debt behavior of young adults, e.g., Rooij, Lusardi, and Alessie (2011); Brown, Grigsby, van der Klaauw, Wenand, and Zafar (2016); and Liberman (2016). Still, it is not entirely clear why marginal dollars of debt would be particularly influential in this regard; moreover, to the extent an information channel is operating, because some of the effect on homeownership occurs contemporaneous to the increase in limits, experience itself cannot fully explain our results. 31 For the remainder of our analyses, we streamline the presentation of results in this manner though the same patterns hold over the years we omit. In particular, there are no statistical differences in either earnings or savings in the year following the year of the discontinuity (Table A.7.), which is most consistent with a liquidity channel. 17

percentage point increase in participation and 1 percent increase in earnings.32 Furthermore, assuming lifetime earnings for college graduates of approximately $2.1 million (College Board, 2016) and even an extremely conservative zero discount rate, our estimates can rule out a lifetime earnings increase of $21,000, suggesting an annual rate of return on marginal grant and loan dollars of less than 5 percent. Finally we do not find effects on more education-centric human capital outcomes, such as completion or enrollment.33 Are these results surprising? While, as noted in the introduction, standard economic models assume student loans help financially constrained individuals make costly educational investments that improve their labor market outcomes, within the empirical literature, even taking into account studies that allow for extensive margin responses, there is, thus far, little evidence that aid affects long-term earnings (e.g., Bettinger et al., 2016). Furthermore, our setting examines marginal dollars made available to student borrowers, among whom there is no evidence of extensive margin (attendance) effects.34 Thus, higher limits would predominantly influence labor outcomes via increases in attainment. While such effects in our environment appear to be negligible, even assuming a large effect, the expected impact on earnings is still small. For example, assume an additional $1,000 leads to a 4 p.p. increase in completion, an estimate on the higher end of the range from the empirical literature (Dynarski, 2003), which was derived from increases in grant aid only (resulting in substantial price effects). If college completion leads to a 15 percent annual increase in earnings, another estimate from the higher end of the empirical literature (CEA, 2016), we would expect our estimated $3,000 increase in grants and loans to increase earnings by, at most, 2 percent. Our estimates are precise enough to rule out such effects. B. Effects on Savings 32 Table A.8 presents alternative specifications for these outcomes, and the results remain similar. 33 Table A.9 analyzes college completion rates, defined cumulatively for each period, and finds no difference at any period over the horizon we examine, overall or splitting the sample by EFC (i.e., according to how otherwise constrained a student borrower is). There are also no short-run effects on enrollment or enrollment intensity (Table A.7). These patterns are consistent with other findings in this section. 34 This is partially by construction, as we omit students at for-profit institutions for whom there is an enrollment effect, although this only applies to a small fraction of students. Denning (2017) finds that access to more aid accelerates completion and some evidence that it reduces earnings in the year of the discontinuity. He finds no effect on earnings in the subsequent year or on completion overall. His design analyzes the effect of the same policy rule we study on all students at four-year colleges in Texas. He restricts the sample to college seniors to examine completion. Stinebrickner and Stinebrickner (2008) find that when college itself is not costly, credit constraints do not hinder completion. 18

We next examine saving behavior as a potential indicator that liquidity drives the homeownership effect. Securing a mortgage generally requires making a down payment and might also entail reserve requirements and/or verifying an established savings pattern. If borrowers are liquidity constrained, they may be unable to meet these basic requirements. Still, a persistent increase in saving would not be particularly consistent with liquidity constraints. Further, evidence of increased saving would provide additional evidence—beyond the lack of effect on enrollment and other education-related outcomes—that marginal student loans and grant dollars are not being (fully) allocated toward education spending. The last column of Figure 6 graphs saving rates for the three representative years. There appears to be a very large difference in the year of the discontinuity that disappears in subsequent years. Indeed, turning to the regression-adjusted estimates in the last column of Table 6, we find that borrowers with higher limits are 2.5 percentage points more likely to save in the year of the discontinuity, with no evidence of an effect in subsequent years, including the year following the year of the discontinuity. We have shown that borrowers with higher limits experience earnings reductions in the year of the discontinuity, so a coincident jump in the saving rate presumably reflects resources acquired through the increased federal support not being immediately allocated toward education, which are then being set aside for future use, placing both the documentation of an account and a down payment within reach. Further, given the rapid decline in the effect after the enrollment year and no increase in investment income in any year in the sample period (a proxy for the amount of savings), those increased resources still appear to be spent quite rapidly, consistent with binding credit constraints.35 C. Results by EFC Next, we try to disentangle liquidity from wealth. Note that the composition of the sample is prima facie evidence of a liquidity channel, as student borrowers are presumably liquidity constrained on some dimension. But, to try to explicitly make this distinction, we first leverage a bright line rule that the DoEd uses to determine an applicant’s EFC. This split also helps isolate the effects of loans and grants. While a lower EFC typically leads to increased grant and loan 35 We examined but did not detect a statistically meaningful difference in the amount of interest and dividend income (a proxy for the level of savings) in any of the years we consider. Effects from the year of, and year following, the discontinuity are presented in table A.7 (as are the effects on the presence of savings). 19

awards, and there are separate EFC formulas for financially dependent and independent applicants, those whose “family income” passes below a certain threshold are automatically assigned a zero EFC. This rule can be used to split the sample into two groups, those who are relatively liquidity constrained and those who experience a relatively large wealth effect. First, borrowers with zero EFC tend to come from lower-income households with fewer assets.36 In addition, this same group would very likely be eligible for the maximum allowable subsidy as financial dependents and thus would be less exposed to a wealth shock in the year of the discontinuity, no matter which side of the threshold their birthdate falls. In other words, relative to the positive EFC group, the zero EFC group primarily experiences higher borrowing limits under the rule.37 Table 7 splits the sample accordingly. In the bottom row, we see that, as expected, borrowing increases substantially for both groups, but the increase in need-based loans and grants for the positive EFC group are each nearly a full order of magnitude larger, whereas most of the effect in the zero EFC group stems from an increase in non-need-based loans. Turning to homeownership, we see that the effect is clearly largest in the zero EFC sample, with the estimates among this group implying an economically significant increase in homeownership in the years of and after the discontinuity.38 Note that all of the coefficients for the positive EFC sample are smaller, none are statistically significant, and the estimates between the groups statistically differ when pooling across all years of analysis. Altogether, responsiveness appears to be concentrated within the group that is eligible for less additional subsidy, favoring the liquidity explanation over the wealth one.39 D. Results Before and After the Great Recession To further examine the role of liquidity, we split the sample into two time periods, leveraging the large change in lending conditions before and after the Great Recession. Specifically, prior to 36 Borrowers from lower-income families are more likely to face credit constraints, both because their parents may be unable to cosign on loans and because they may be unable to rely on family resources for funding or collateral (Souleles, 2000; Johnson, Parker, and Souleles, 2006; Sun and Yannelis, 2016). 37 Moreover, responsiveness within the zero EFC group is less likely to be driven by human capital effects (at least those that stem from an increase in subsidy). 38 Table A.10 repeats the analysis for the labor market outcomes and shows there is no evidence in either group of an effect in later years, nor do the conclusions change when we winsorize labor earnings or only include linear splines in the specifications (not shown), further evidence that human capital effects do not drive our main estimates. 39 As further evidence, in Table A.11, we split the sample by school type and find effects are largest among borrowers attending public universities and two-year colleges, which tend to draw students from lower-income backgrounds. Table A.12 shows that the effects on loans and grants are pronounced across all school types. 20

2007, underwriting standards were relatively lax and credit was more widely available (Keys et al., 2008; Keys, Seru, and Vig, 2012). The effects of the crisis permeated the entire credit market. Fostel and Geanakoplos (2016) note that the average down payment for subprime home loans went from approximately 3 percent in the first quarter of 2006 to 16 percent in the first quarter of 2008. Figure A.6 shows that the fraction of banks tightening lending standards for consumer loans sharply increased in 2007. Finally, household balance sheets and local labor market conditions suffered as well. Given these factors, if liquidity effects are driving our results, we would expect to see the largest responses when conditions are tightest (i.e., beginning in 2007).40 We begin by splitting the sample into whether the year of the discontinuity occurred before or after the contraction of credit, dividing borrowers enrolled through 2006 and borrowers enrolled in 2007 onward.41 The left-hand columns of Table 8 indicate that the homeownership effect is an order of magnitude larger and only statistically significant during the crisis, consistent with a liquidity explanation. Still, a potential concern is that the composition of borrowers changed between the two periods, which could be driving the differences in our estimates (Looney and Yannelis, 2015). To address this concern, we repeat the analysis for borrowers enrolled in 2007 onward, reweighting the sample by demographics to resemble borrowers in the earlier period. The results are quite similar to those before, with the estimated effect on homeownership still highly significant. Finally, to further explore a possible liquidity channel, we split the recessionary sample into EFC groups under the same premise as the last EFC exercise—i.e., that those with zero EFC are more constrained and primarily experience increases in their borrowing limits, with relatively little increase in their subsidy. The final columns imply that, when credit conditions were extraordinarily tight, the response is still concentrated within this group. In sum, our analysis of mechanisms indicates that the main estimates are driven by increased liquidity rather than by human capital or wealth effects. Further, while not shown, there is also no evidence of differences in debt cancellation measured by Form 1099-C filings (e.g., debt discharge, bankruptcy) over the full study horizon, consistent with these early career liquidity injections being 40 Housing prices also decreased between these two periods, which might compound any effect on liquidity stemming from changing credit conditions. 41 We do not include results for later years, as for some borrowers assigned to the prior period in this exercise, later outcomes will be observed during the recession, which would make their interpretation difficult. Further, data becomes unavailable the further out we go for cohorts in the post period. Nonetheless, the results are similar in later years. 21

net beneficial to student borrowers over the horizon we examine. In addition, homeownership itself may offer a future source of liquidity. Our findings imply that, on balance, limit increases help alleviate financial constraints that young adults face and make them better able to smooth consumption between time periods.42 VI. Family Formation We round out the analysis by examining marriage and fertility rates to probe whether the increases in homeownership we detect point to more general increases in household formation, which may similarly entail upfront fixed costs. As with homeownership rates, some commentators have expressed concerns that family formation is depressed among young college graduates due to high student debt balances.43 Figure 7 shows these outcomes for the three representative years. Note that any differences in the year of the discontinuity are very small; however, they evolve over time and are reasonably stark by the end of the medium run. The regression-adjusted estimates in Table 9 largely corroborate the graphical evidence.44 Neither effect is statistically significant in the year of the discontinuity, though both effects grow over the medium run. Indeed, it appears that both marriage and fertility lag the initial homeownership effect, such that, by the middle of the horizon, borrowers with higher limits are more likely to be married and more likely to have had children. VII. Concluding Remarks We find that additional access to federal student loans and grants increases homeownership and family formation among student borrowers, with little effect on their human capital. Effects are concentrated among those from low-income households and with lower levels of family wealth, as well as during periods when other forms of credit were relatively unavailable. While the policy rule induces both an increase in borrowing limits and an increase in subsidies, effects appear to be driven by the former. Altogether, our results demonstrate that these programs, particularly the student lending program, serve an important credit function, enhancing the liquidity of an 42 While Yannelis (2016) finds that increased student borrowing can induce student loan default, within our setting, any adverse consequences for liquidity from this channel appear to be dominated by other more liquidity-beneficial channels (e.g., direct resource effects), which may partly owe to the exclusion of for-profit borrowers from our sample. 43 Moreover, it may be that homeownership itself has real effects on these outcomes (Sodini, Vestman, and von Lilienfeld-Toal, 2017). 22

otherwise highly constrained group (i.e., young adults). This implication adds dimensionality to the popular narrative around the student loan program—challenging the belief that, outside of potential human capital benefits, it largely hurts or delays household formation—and a new consideration to cost-benefit analyses of student aid programs more generally. To help with interpretation, our estimates can be combined to yield a suggestive estimate of the effect of additional student loan and grant dollars on homeownership. In particular, scaling the homeownership estimate by the estimated effect on federal student loans and grants implies that an additional $10,000, on average, raises homeownership by 2.4 p.p. (i.e., over 10 percent of the sample mean).45 We can compare this estimate to those implied by Bulman et al. (2017), which examines lottery wins among parents of post-adolescent children. This study, while similar to our design in estimating the effect of cash on hand, draws upon older age ranges and already-formed families. Unsurprisingly, our effects are larger, though not extremely so: Their estimates imply a 0.8 p.p. increase in homeownership for a range in which the mean win was about $15,000 and a 4 p.p. increase for a range in which the mean win was about $50,000.46 Our results underscore the importance of understanding the origins of student debt when assessing its implications for the economy. While the potential financial stress that such debt poses on young households has dominated the discussion, the net returns from the activities that the original loans were used to finance should be the first-order consideration. As our study illuminates, in addition to whether student borrowers have seen positive net returns from the education that they financed with loans, policymakers must also consider whether they separately extracted liquidity from these loans to finance non-education spending that ultimately left them better off as well. Future research should consider such effects when assessing the welfare consequences of these programs. (That said, our particular context points to potentially negative 45 A causal interpretation of this estimate requires an assumption—namely, that homeownership is only influenced by the policy rule through its effect on federal student loans and grants—that may not hold. However, note that if higher federal student loan and grant limits crowd out (in) other forms of financial aid, the effect of the marginal financial aid dollar is larger (smaller) than this calculation implies. 46 Alternatively, we can compare it to a recent estimate from the housing literature. Berger, Turner, and Zwick (2016) examine the First-Time Homebuyer Credit (FTHC), a temporary tax credit for new homebuyers intended to stimulate home purchases between 2008 and 2010. Their study analyzes a policy targeted toward homeownership but draws upon age ranges and cohorts similar to those we examine; however, it entails broader price effects on the housing market that will dampen the individual partial-equilibrium effects. They find that the more generous phases of the FTHC—during which the maximum credit was $8,000—induced as many as 546,000 home sales, which, based on our calculations, implies a 2.3 p.p. increase in homeownership. (The denominator for this calculation is the number of tax returns filed by 26–35 year olds in 2008 published by the IRS Statistics of Income in July 2010.) 23

net returns from the small amount of additional educational investment being financed with loans, which was concentrated within for-profit colleges.) Increasing homeownership has been a central policy goal in the United States, often motivated by potential consumption benefits and positive social externalities of owning a home. The federal government spends at least $70 billion a year on the mortgage interest deduction under the auspices that it will encourage homeownership, even though in present day, the majority of spending finances intensive margin housing decisions with few such benefits (e.g., Glaeser and Shapiro, 2003) and the hazard rate into homeownership among young people has been declining (Bhutta, 2015). Policies that more efficiently stimulate homeownership may thus be of interest. Finally, our findings have implications for models of human capital formation that allow prospective students to be financially constrained. These models are a major rationale for student lending programs, which theoretically enable costly educational investments associated with positive net labor market returns. With the exception of a negative effect on earnings within the year of the discontinuity, our estimates imply that higher borrowing limits generally do not affect earnings, labor force participation, or college completion, calling into question how policymakers should motivate proposed increases in limits. Moreover, effects on enrollment are concentrated within a notoriously low return sector. Thus, our results are not particularly consistent with financial constraints stymieing optimal investment in education, at least along the margins we consider.47 Nonetheless, we caution that our estimates represent the effects of marginal changes in program limits among a specific population of student borrowers, those who turn 24 years old while enrolled. This population may tend to graduate over longer horizons or enter late. Large changes in limits or changes that affect other populations could generate different effects. For example, enrollment and completion effects could be much more substantial during earlier lifecycle phases when educational investments are potentially more sensitive. Furthermore, it is possible that, while higher limits, on balance, alleviate constraints over the horizon we study, 47 That said, the human capital benefits of higher limits may be being offset by another underlying process. Debt may pose a drag on labor outcomes (Liberman, 2016; Dobbie et al., 2016; Herkenhoff, 2013) or disincentivize work in a manner similar to income taxation (Bernstein, 2016; Donaldson, Piacentino, and Thakor, 2016; Mondragon, 2017). Or, schools may price discriminate and raise tuition in lockstep with loan and grant limits (Cellini and Goldin, 2014; Lucca, Nadauld, and Shen, 2017; Turner, 2017). Finally, education may have unobservable consumption value (Lazear, 1977) and generate externalities (Moretti, 2004a and 2004b), which could entail human capital effects beyond those that we consider. 24

higher debt levels may play a role in exacerbating liquidity constraints later in life. Future research should examine liquidity effects of the federal student loan and grant programs within other populations and environments and on other spending outcomes. 25

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stceffEtnemllornErofgnitseT&noitcurtsnoCelpmaS :1erugiF hcaeevobadetonedsiemoctuoehT .ytiunitnocsidehtforaeyehtnielbairavtnemngissaehtfosnibyad-02nistnedutsforebmunnaemehtswohserugfisihT :setoN tfiorpnonetavirptasreworrobswohslenapthgirehtdna,snoitutitsnicilbuptasreworrobswohslenapelddimeht,sreworrobtfiorp-rofswohslenaptfelehT .etamitse atadtnemllornE.atadxatSRImorfemocatadllA.ytiunitnocsidehtforaeyradnelacehtni42gninrutmorfsyadforebmunehtsielbairavtnemngissaehT.snoitutitsni .smrofT-8901morfera tnemllornEtfiorP-noNetavirP tnemllornEcilbuP tnemllornEtfiorP-roF 062 052 042 032 tnuoC 001 05 0 05- 001ffotuC morf syaD 0091 0581 0081 0571 0071 tnuoC 001 05 0 05- 001ffotuC morf syaD 083 063 043 023 003 tnuoC 001 05 0 05- 001ffotuC morf syaD 32

Figure2: DensityofBorrowers Notes: This figure shows density of the assignment variable, in bins of 20 days from dependency cutoff, for the final analysis sample. The assignment variable is the number of days from turning 24 in the calendar year of the discontinuity. Borrowersinthedonutholeareexcluded,asdiscussedinthetext. TheMcCrary(2008)teststatisticis .1052(.4956).AlldatacomefromtheNSLDSmatchedtoIRStaxdata. tnuoC 00001 0058 0007 0055 0004 -200 -100 0 100 200 Days from Cutoff 33

Figure3: EffectofLimitIncreaseonFederalLoansandGrants Notes:Thisfigureshowsmeanestimatesofthelimitincreaseonloansandgrantsintheyearofthediscontinuityin20-day binsoftheassignmentvariable,brokendownbythedifferenttypeofloanorgrant. Theoutcomeisdenotedaboveeach estimate. Theassignmentvariableisthenumberofdaysfromturning24inthecalendaryearofthediscontinuity. All datacomefromtheNSLDSmatchedtoIRStaxdata. FederalLoans FederalLoansandGrants snaoL latoT 0008 0057 0007 0056 0006 -100 -50 0 50 100 Days from Cutoff stnarG dna snaoL latoT 00021 00011 00001 0009 0008 -100 -50 0 50 100 Days from Cutoff Non-NeedBasedLoans NeedBasedLoans snaoL desaB deeN-noN 0023 0003 0082 0062 0042 -100 -50 0 50 100 Days from Cutoff snaoL desaB deeN 0005 0054 0004 0053 -100 -50 0 50 100 Days from Cutoff PellGrants lleP 0052 0002 0051 0001 -100 -50 0 50 100 Days from Cutoff 34

Figure4: Homeownership Notes:Thisfigureshowsmeanhomeownershipin20-daybinsoftheassignmentvariable,definedbythepresenceof amortgage. Theassignmentvariableisthenumberofdaysfromturning24inthecalendaryearofthediscontinuity. AlldatacomefromtheNSLDSmatchedtoIRStaxdata. YearofDiscontinuity OneYearPostDiscontinuity egagtroM 60. 550. 50. -100 -50 0 50 100 Days from Cutoff egagtroM 11. 501. 1. 590. -100 -50 0 50 100 Days from Cutoff TwoYearsPostDiscontinuity . ThreeYearsPostDiscontinuity egagtroM 71. 561. 61. 551. 51. -100 -50 0 50 100 Days from Cutoff egagtroM 532. 32. 522. 22. -100 -50 0 50 100 Days from Cutoff FourYearsPostDiscontinuity FiveYearsPostDiscontinuity egagtroM 892. 692. 492. 292. 92. 882. -100 -50 0 50 100 Days from Cutoff egagtroM 653. 453. 253. 53. 843. -100 -50 0 50 100 Days from Cutoff 35

Figure5: AlternativeBandwidthforHomeownership Notes: This figure shows point estimates and a 95% confidence interval from the regression discontinuity design, varying bandwidth. The horizontal axis denotes the assigned bandwidth. Specifications include a quadratic spline of the assignment variable, which is the number of days from turning 24 in the calendar year of the discontinuity. Standarderrorsareclusteredatthedayfromcutofflevel.AlldatacomefromtheNSLDSmatchedtoIRStaxdata. YearofDiscontinuity OneYearPostDiscontinuity 20. 510. 10. 500. 0 500.- 20 40 60 80 Bandwidth 30. 20. 10. 0 10.- 20 40 60 80 Bandwidth TwoYearsPostDiscontinuity ThreeYearsPostDiscontinuity 30. 20. 10. 0 10.- 20.- 20 40 60 80 Bandwidth 60. 40. 20. 0 20.- 20 40 60 80 Bandwidth FourYearsPostDiscontinuity FiveYearsPostDiscontinuity 60. 40. 20. 0 20.- 20 40 60 80 Bandwidth 60. 40. 20. 0 20.- 20 40 60 80 Bandwidth 36

Figure6: HumanCapitalandSavings Notes: Thisfigureshowsmeanoutcomesin20-daybinsoftheassignmentvariableintheyearofthediscontinuity,three yearsaftertheyearofthediscontinuity,andfiveyearsaftertheyearofthediscontinuity.Thedependentvariableinthefirst columniswageearnings. Thedependentvariableinthesecondcolumnisanindicatordenotingwhetherwageearnings arereportedonbehalfofanindividual.Thedependentvariableinthethirdcolumnisanindicatorofwhetheranindividual hasinterestordividendincome. Theoutcomeisdenotedaboveeachestimate. Theassignmentvariableisthenumberof daysfromturning24inthecalendaryearofthediscontinuity.AlldatacomefromtheNSLDSmatchedtoIRStaxdata. Wages Works Savings YearofDiscontinuity segaW 00531 05231 00031 05721 00521 05221 -100 -50 0 50 100 Days from Cutoff kroW 29. 519. 19. 509. 9. -100 -50 0 50 100 Days from Cutoff tnuoccA sgnivaS 532. 522. 512. 502. -100 -50 0 50 100 Days from Cutoff ThreeYearsPostDiscontinuity segaW 00092 00082 00072 -100 -50 0 50 100 Days from Cutoff kroW 49. 39. 29. 19. 9. -100 -50 0 50 100 Days from Cutoff tnuoccA sgnivaS 82. 72. 62. 52. 42. 32. -100 -50 0 50 100 Days from Cutoff FiveYearsPostDiscontinuity segaW 00543 00043 00533 00033 00523 -100 -50 0 50 100 Days from Cutoff kroW 39. 29. 19. 9. 98. -100 -50 0 50 100 Days from Cutoff tnuoccA sgnivaS 3. 92. 82. 72. 62. -100 -50 0 50 100 Days from Cutoff 37

Figure7: MarriageandChildren Notes: This figure shows mean marriage and children in 20-day bins of the assignment variable. The dependent variableinthefirstcolumnisanindicatordenotingwhetheranindividualismarried. Thedependentvariableinthe secondcolumnisanindicatorofwhetheranindividualhashadachild. Theoutcomeisdenotedaboveeachestimate. "Children"referstoanindicatorofwhetheraborrowerhashadanychildrenbythatyear. Theassignmentvariableis thenumberofdaysfromturning24inthecalendaryearofthediscontinuity.AlldatacomefromtheNSLDSmatched toIRStaxdata. Spouse Children YearofDiscontinuity YearofDiscontinuity esuopS 531. 521. 511. 501. -100 -50 0 50 100 Days from Cutoff sdiK 40. 30. 20. 10. -100 -50 0 50 100 Days from Cutoff ThreeYearsPostDiscontinuity ThreeYearsPostDiscontinuity esuopS 513. 13. 503. 3. 592. -100 -50 0 50 100 Days from Cutoff sdiK 71. 561. 61. 551. 51. 541. 41. -100 -50 0 50 100 Days from Cutoff FiveYearsPostDiscontinuity FiveYearsPostDiscontinuity esuopS 24. 514. 14. 504. 4. -100 -50 0 50 100 Days from Cutoff sdiK 82. 572. 72. 562. 62. -100 -50 0 50 100 Days from Cutoff 38

Table1: SummaryStatistics Notes: This table shows summary statistics. Each variable is listed in the left-most column, along with the mean, standard deviation, and number of observations. The year after the discontinuity is listed beneath outcome variables. All data come from theNSLDSmatchedtoIRStaxdata Mean SD Observations Loans 6,777.65 3,635.31 464,008 Need Based 4,019.61 2,528.30 464,008 Non-Need Based 2,758.04 2,886.84 464,008 Pell Grants 1,842.21 1,967.78 464,008 Mortgage Year 0 0.05 0.23 464,008 1 0.10 0.30 464,008 2 0.16 0.36 464,008 3 0.22 0.41 426,478 4 0.29 0.45 388,518 5 0.34 0.48 352,446 Wages Year 0 12,944.08 12,105.31 464,008 3 28,140.90 30,181.70 426,478 5 33,380.50 28,057.64 352,446 Works Year 0 0.91 0.29 464,008 3 0.92 0.27 426,478 5 0.90 0.29 352,446 Savings Year 0 0.21 0.41 464,008 3 0.24 0.43 426,478 5 0.27 0.44 352,446 Spouse Year 0 0.11 0.32 464,008 3 0.30 0.46 426,478 5 0.40 0.49 352,446 Children Year 0 0.02 0.28 464,008 3 0.16 0.52 426,478 5 0.27 0.70 352,446 Frequency Academic Year 2 15.78 3 22.36 4 49.10 5 12.76 39

Table2: PredeterminedCovariates Notes: This table shows regression discontinuity estimates of predeterminedoutcomesandcovariates. Eachvariableisdenotedabovetheestimates. Ingeneral,astime-varyingtaxvariablespertaintocalendaryears and t-1 measures may partially reflect treatment, balance over such variablesistestedusingt-2measures;time-varyingeducationvariablespertain toacademicyearsandthusbalanceoversuchvariablesistestedusingthe prior academic year. (Academic level, four-year, and public enrollment, over which the primary concern would be sorting, are tested using measures in t.) The analysis of whether the borrower filed the FAFSA as an independent before adds those borrowers back in the sample. Although not entirely exogenous, calendar year outcomes are also insignificant in t-1.Forexample,theestimateonmortgagesis-0.0003withastandarderrorof0.0018. Specificationsincludeaquadraticsplineoftheassignment variable,whichisthenumberofdaysfromturning24inthecalendaryear of the discontinuity. Standard errors are clustered at the day from cutoff level. AlldatacomefromtheNSLDSmatchedtoIRStaxdata. *p < .1, **p<.05,***p<.01. (1) (2) (3) Mortgage Savings Family Income Above Cutoff .0015612 .0015762 .0096111 (.0015204) (.0029899) (.0149399) Works Wages Children Above Cutoff 0002253 313.645 -.0023549 (.0034927) (208.1957) (.0038721) US Citizen Gender Borrowed Above Cutoff .0009799 .0110338* .0225669 (.0029496) (.005637) (.0233396 ) Acad. Level Public Spouse Above Cutoff -.0106153 .0049528 -.0013308 (.0101294) (.0044997) (.0110233 ) Independent Zero EFC FourYear Above Cutoff .004094 .0003425 -.0048781 (.0044181) (.005113) (.0030946) 40

stnarGdnasnaoLlaredeFnoesaercnItimiLfotceffE :3elbaT ehtforaeycimedacaehtnitpiecertnargdnanaollaredeffosetamitseytiunitnocsidnoissergerswohselbatsihT :setoN tnemngissaehtfoenilpscitardauqaedulcnisnoitacfiicepS .setamitseehtevobadetonedsielbairavhcaE .ytiunitnocsid ehtmorfemocatadllA .ytiunitnocsidehtforaeyradnelacehtni42gninrutmorfsyadforebmunehtsihcihw,elbairav .10.<p***,50.<p**,1.<p*.atadxatSRIotdehctamSDLSN stnarG lleP dna snaoL laredeF snaoL latoT lleP desaB deeN-noN desaB deeN latoT stnarG dna stnarG snaoL laredeF snaoL laredeF snaoL laredeF )5( )4( )3( )2( )1( ***796.572,3 ***718.233,1 ***20783.266 ***135.032,1 ***819.298,1 ffotuC evobA )66182.85( )83914.42( )588892.84( )192935.93( )318011.44( 800,464 800,464 800,464 800,464 800,464 snoitavresbO 41

setamitsEpihsrenwoemoH :4elbaT ehtfoenilpscitardauqaedulcnisnoitacfiicepS .sraeyretaldnaytiunitnocsidehtforaeyehtnisetamitseytiunitnocsidnoissergerswohselbatsihT :setoN morfyadehttaderetsulcerasrorredradnatS .ytiunitnocsidehtforaeyradnelacehtni42gninrutmorfsyadforebmunehtsihcihw,elbairavtnemngissa .10.<p***,50.<p**,1.<p*.atadxatSRIotdehctamSDLSNehtmorfemocatadllA.levelffotuc )6( )5( )4( )3( )2( )1( retfA sraeY eviF retfA sraeY ruoF retfA sraeY eerhT retfA sraeY owT retfA raeY fo raeY nI ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD 2850900. **7237010. **95110.0 **3827800. **3803700. **542500. ffotuC evobA )820600.0( )864500.0( )269400.( )259300.( )893300.( )483200.( 644,253 815,883 874,624 800,464 800,464 800,464 snoitavresbO 42

selpmaSobecalPnipihsrenwoemoH :5elbaT ybdetceffanuerewtahtspuorgrofsraeyretaldnaytiunitnocsidehtforaeyehtnisetamitseytiunitnocsidnoissergerswohselbatsihT:setoN raeyehtnitontub,sraeyrehtonisnaoltuokootohwslaudividnifoelpmasmodnararofsisylanaehtstaeperlenappoteht.ytiunitnocsideht elpmasruotfiesiwrehtotub,42gninruterofebstnednepednisaASFAFehtdelfiohwsreworrobswohslenapmottobehT .42nrutyehttaht ehtni42gninrutmorfsyadforebmunehtsihcihw,elbairavtnemngissaehtfoenilpscitardauqaedulcnisnoitacfiicepS .airetircnoitceles SRIotdehctamSDLSNehtmorfemocatadllA.levelffotucmorfyadehttaderetsulcerasrorredradnatS.ytiunitnocsidehtforaeyradnelac .10.<p***,50.<p**,1.<p*.atadxat stseT obecalP )6( )5( )4( )3( )2( )1( sraeY rehtO ni deworroB ylnO retaL sraeY eviF retaL sraeY ruoF retaL sraeY eerhT retaL sraeY owT retaL raeY enO raeY ytiunitnocsiD 8411300. 592400. 6675200. 7640200. 1676100. 8524200.ffotuC evobA )696400.( )2374400.( )9841400.( )386300.( )9483300.( ) 2671300.( 671,665 586,416 782,466 716,417 716,417 716,417 snoitavresbO tnednepednI ydaerlA retaL sraeY eviF retaL sraeY ruoF retaL sraeY eerhT retaL sraeY owT retaL raeY enO raeY ytiunitnocsiD 9426100. 6543100. 4373300.- 19000.- 419800.- 5577000.ffotuC evobA )902210.( )9873210.( )9491110.( ) 2524010.( )1774900.( )5666800.( 092.19 194,101 658,211 118,421 118,421 118,421 snoitavresbO 43

Table6: HumanCapitalandSavings Notes: Thistableshowsregressiondiscontinuityestimatesintheyearofthediscontinuity,threeyearsaftertheyearofthediscontinuity,andfiveyearsafterthe yearofthediscontinuity. Thedependentvariableinthefirstcolumnisearnings. Thedependentvariableinthesecondcolumnisanindicatordenotingwhetheran individualreportsanyearnings. Thedependentvariableinthethirdcolumnisan indicatordenotingwhetheraborrowerhasinterestordividendincome.Specificationsincludeaquadraticsplineoftheassignmentvariable,whichisthenumberof daysfromturning24inthecalendaryearofthediscontinuity.Standarderrorsare clusteredatthedayfromcutofflevel.AlldatacomefromtheNSLDSmatchedto IRStaxdata.*p<.1,**p<.05,***p<.01. Wages Works Savings (1) (2) (3) Year of Discontinuity Above Cutoff -240.2872* -.0027539 .0248975*** (130.9886) (.0030782) (.0048689) Observations 464,008 464,008 464,008 Three Years Later Above Cutoff -234.3991 -.0018542 -.0055291 (275.9309 ) (.0030866) (.0050734) Observations 426,478 426,478 426,478 Five Years Later Above Cutoff -323.4143 -.0008361 -.0019679 (338.6448) (.0037454) (.0031079) Observations 352,446 352,446 352,446 44

CFEoreZybpihsrenwoemoH :7elbaT retfasraeyevfidna,ytiunitnocsidehtforaeyehtretfasraeyeerht,ytiunitnocsidehtforaeyehtnisetamitseytiunitnocsidnoissergerswohselbatsihT :setoN naol susrev tnarg stceffa dna htlaew dna emocni ylimaf ni secnereffid stcefler sutats CFE oreZ .CFE oreznon ro orez a yb nwod nekorb ,ytiunitnocsid eht .tnacfiingisnierapuorgsihtnostceffeeht;sisylanasihtmorfdedulcxeeradnaraeyroirpehtniASFAFaelfitondidelpmasehtfo%51tuobA .ytilibaliava morfsyadforebmunehtsihcihw,elbairavtnemngissaehtfoenilpscitardauqaedulcnisnoitacfiicepS .stnargdnasnaolnotceffeehtswohswormottobehT SRIotdehctamSDLSNehtmorfemocatadllA .levelffotucmorfyadehttaderetsulcerasrorredradnatS .ytiunitnocsidehtforaeyradnelacehtni42gninrut .10.<p***,50.<p**,1.<p*.atadxat )6( )5( )4( )3( )2( )1( 0>CFE CFE oreZ retfA sraeY eviF retfA sraeY eerhT fo raeY retfA sraeY eviF retfA sraeY eerhT fo raeY ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD 9903700.0 3812800.0 257400. 7960910.0 ***5184030.0 *7867800. ffotuC evobA )5896600.0( ) 9882600.0( ) 1971300.0( )9264310.0( )2854900.0( )3847400.( stnarG dna snaoL no tceffE stnarG dna snaoL no tceffE stnarG lleP snaoL desaB deeN snaoL deeN-noN stnarG lleP snaoL desaB deeN snaoL deeN-noN ***765.948,1 ***291.284,1 ***6336.635 ***112.902 ***825.592 ***714.134,1 ffotuC evobA )45990.84( )30468.34( )76897.55( )16703.56( )56294.65( )76827.17( 076,732 232,082 738,203 395,35 830,87 096,09 snoitavresbO 45

doirePemiTybpihsrenwoemoH :tiderCfoytilibaliavA :8elbaT ,sraeyreilraedna6002nisemoctuoswohsnmuloctsrfiehT .6002retfadnaerofeb,ytiunitnocsidehtforaeyehtnisetamitseytiunitnocsidnoissergerswohselbatsihT :setoN edulcnisnoitacfiicepS.levelcimedacadnascihpargomedybelpmasehtshgiewernmulocdrihtehT.7002gnidulcnidnaretfasemoctuowohssnmulocdrihtdnadnocesehtelihw morfyadehttaderetsulcerasrorredradnatS.ytiunitnocsidehtforaeyradnelacehtni42gninrutmorfsyadforebmunehtsihcihw,elbairavtnemngissaehtfoenilpscitardauqa .10.<p***,50.<p**,1.<p*.atadxatSRIotdehctamSDLSNehtmorfemocatadllA.levelffotuc )5( )4( )3( )2( )1( )CFE evitisoP( retaL dna 7002 )CFE oreZ( retaL dna 7002 )dethgieW( retaL dna 7002 retaL dna 7002 reilraE dna 6002 ytiunitnocsiD fo raeY ytiunitnocsiD fo raeY ytiunitnocsiD fo raeY ytiunitnocsiD fo raeY ytiunitnocsiD fo raeY 1538500. ***8916510. ***910900. ***5454900. 6906000. ffotuC evobA )4305400. ( )9827500.( )171300.( )6731300.( )7085300.( 073,941 049,26 594,242 594,242 315,122 snoitavresbO 46

semoctuOnoitamroFylimaF :9elbaT -sidehtforaeyehtnisetamitseytiunitnocsidnoissergerswohselbatsihT :setoN ehtretfasraeyevfidna,ytiunitnocsidehtforaeyehtretfasraeyeerht,ytiunitnoc arehtehwsinmuloctsrfiehtnielbairavtnednepedehT .ytiunitnocsidehtforaey rotacidninasinmulocdnocesehtnielbairavtnednepedehT.deirramsireworrob snoitacfiicepS .detacidni raey eht yb nerdlihc dah sah laudividni na rehtehw fo syadforebmunehtsihcihw,elbairavtnemngissaehtfoenilpscitardauqaedulcni -sulcerasrorredradnatS.ytiunitnocsidehtforaeyradnelacehtni42gninrutmorf SRIotdehctamSDLSNehtmorfemocatadllA.levelffotucmorfyadehttaderet .10.<p***,50.<p**,1.<p*.atadxat )2( )1( ytiunitnocsiD fo raeY nerdlihC deirraM 3048100. 1844000. ffotuC evobA )9505100.( )836300.( 800,464 800,464 snoitavresbO retaL sraeY eerhT nerdlihC deirraM *5023700. **5285110. ffotuC evobA )8411400.( )6195500.( 874,624 874,624 snoitavresbO retaL sraeY eviF nerdlihC deirraM **5240310. **5548310. ffotuC evobA )3951600.( )3875600.( 815,883 815,883 snoitavresbO 47

FigureA.1: DensityofBorrowers Notes: This figure shows number of borrowers by the assignment variable, in bins of nine days from dependency cutoff. Theassignmentvariableisthenumberofdaysfromturning24inthecalendaryearofthediscontinuity. All datacomefromtheNSLDSmatchedtoIRStaxdata. tnuoC 0005 0004 0003 0002 0001 0 -200 -100 0 100 200 Days from Cutoff 48

FigureA.2: PredeterminedVariablesAlongCutoff Notes: This figure shows mean outcome variables in the pre-period in 20-day bins of the assignment variable. The outcome is denoted above each estimate. The assignment variable is the number of days fromturning24inthecalendaryearofthediscontinuity. AlldatacomefromtheNSLDSmatchedtoIRS taxdata. Mortgaget−2 Savingst−2 egagtroM 40. 30. 20. 10. 0 -100 -50 0 50 100 Days from Cutoff sgnivaS 32. 22. 12. 2. 91. -100 -50 0 50 100 Days from Cutoff Workst−2 Wagest−2 skroW 58. 38. 18. 97. 77. 57. -100 -50 0 50 100 Days from Cutoff segaW 0009 0008 0007 -100 -50 0 50 100 Days from Cutoff Spouset−2 Childrent−2 esuopS 40. 30. 20. 10. 0 -100 -50 0 50 100 Days from Cutoff shtriB 20. 510. 10. 500. 0 -100 -50 0 50 100 Days from Cutoff 49

stnarGdnasnaoLnoesaercnItimiLfotceffErofhtdiwdnaBevitanretlA :3.AerugiF gniyrav,ngisedytiunitnocsidnoissergerehtmorflavretniecnedfinoc%59adnastnargdnasnaolnoesaercnitimilehtfotceffeehtrofsetamitsetniopswohserugfisihT :setoN ,elbairavtnemngissaehtfoenilpsraenilaedulcnisnoitacfiicepS .etamitsehcaeevobadetonedsiemoctuoehT .htdiwdnabdengissaehtsetonedsixalatnozirohehT .htdiwdnab SDLSNehtmorfemocatadllA .levelffotucmorfyadehttaderetsulcerasrorredradnatS .ytiunitnocsidehtforaeyradnelacehtni42gninrutmorfsyadforebmunehtsihcihw .atadxatSRIotdehctam stnarGlleP snaoLdesaBdeeN snaoLdesaBdeeN-noN 057 007 056 006 055 08 06 04 02 htdiwdnaB 0531 0031 0521 0021 0511 08 06 04 02 htdiwdnaB 0541 0041 0531 0031 08 06 04 02 htdiwdnaB 50

FigureA.4: AlternativeBandwidthforHomeownershipResultsUsingLinearSpline Notes: Thisfigureshowspointestimatesanda95%confidenceintervalfromtheregressiondiscontinuitydesign,varying bandwidth. Thehorizontalaxisdenotestheassignedbandwidth. Specificationsincludealinearsplineoftheassignment variable,whichisthenumberofdaysfromturning24inthecalendaryearofthediscontinuity.Standarderrorsareclustered atthedayfromcutofflevel.AlldatacomefromtheNSLDSmatchedtoIRStaxdata. YearofDiscontinuity OneYearPostDiscontinuity 10. 500. 0 20 40 60 80 Bandwidth 510. 10. 500. 0 20 40 60 80 Bandwidth TwoYearsPostDiscontinuity . ThreeYearsPostDiscontinuity 20. 510. 10. 500. 0 500.- 20 40 60 80 Bandwidth 30. 20. 10. 0 10.- 20 40 60 80 Bandwidth FourYearsPostDiscontinuity FiveYearsPostDiscontinuity 30. 20. 10. 0 10.- 20 40 60 80 Bandwidth 30. 20. 10. 0 10.- 20 40 60 80 Bandwidth 51

FigureA.5: PlaceboCutoffs: Mortgages Notes: Thisfigureshowspointestimatesanda95%confidenceintervalfromtheregressiondiscontinuitydesign,varying theassignedcutoff. Thehorizontalaxisdenotestheassignedcutoff. Theoutcomesismortgagesintheyearlistedabove each panel. Specifications include a quadratic spline of the assignment variable, which is the number of days from the assigned cutoff. Given the donut hold nature of our design, the placebo discontinuities within three days of the actual discontinuityhavethesamecutoffbutslightlydifferentbandwidths. Standarderrorsareclusteredatthedayfromcutoff level.AlldatacomefromtheNSLDSmatchedtoIRStaxdata. YearofDiscontinuity OneYearPostDiscontinuity etamitsE 10. 500. 0 500.- 10.- 30 15 0 -15 -30 Distance etamitsE 20. 10. 0 10.- 20.- 30 15 0 -15 -30 Distance TwoYearsPostDiscontinuity . ThreeYearsPostDiscontinuity etamitsE 20. 10. 0 10.- 20.- 30 15 0 -15 -30 Distance etamitsE 20. 10. 0 10.- 20.- 30 15 0 -15 -30 Distance FourYearsPostDiscontinuity FiveYearsPostDiscontinuity etamitsE 20. 10. 0 10.- 20.- 30 15 0 -15 -30 Distance etamitsE 20. 10. 0 10.- 20.- 30 15 0 -15 -30 Distance 52

FigureA.6: FractionofBanksTighteningConsumerCredit Notes: Thisfigureshowsthenetpercentageofbankstighteningstandardsforconsumerloansandcreditcardseachyear between2006and2010.ThesourceistheFederalReserveBankofSt.Louis. tiderC remusnoC gninethgiT sknaB fo .carF 06 04 02 0 02- Jan 2006 Jan 2007 Jan 2008 Jan 2009 53

TableA.1: BorrowingLimitsforFederalStudentLoanPrograms Notes: Thetabledescribesthestatutorylimitsforthefederalstudentloanprogramssince1994forneed-based andnon-need-basedloansbydependencystatusandacademiclevel. Recent Stafford Loan Limits Financial Dependency Status Level Dependent Independent Cumulative Cumulative (Subsidized (Subsidized and and Subsidized Unsubsidized) Subsidized Unsubsidized) 2008-Present First Year $3,500 $5,500 $3,500 $9,500 Second Year $4,500 $6,500 $4,500 $10,500 Third Year and Above $5,500 $7,500 $5,500 $12,500 Lifetime $23,000 $31,000 $23,000 $57,500 2007-2008 First Year $3,500 $3,500 $3,500 $7,500 Second Year $4,500 $4,500 $4,500 $8,500 Third Year and Above $5,500 $5,500 $5,500 $10,500 Lifetime $23,000 $23,000 $23,000 $46,000 1994-2007 First Year $2,625 $2,625 $2,625 $6,625 Second Year $3,500 $3,500 $3,500 $7,500 Third Year and Above $5,500 $5,500 $5,500 $10,500 Lifetime $23,000 $23,000 $23,000 $46,000 54

tnemllornE :2.AelbaT siepytnoitutitsnI .tnemllornegolnoesaercnitimilehtfotceffeehtfosetamitseswohselbatsihT :setoN hcaenielbairavtnednepedehT.ffotucmorfyadehtotdespallocneebsahataD.lenaphcaeevobadetoned ffotucmorfyadehttaderetsulcerasrorredradnatS.dellorneslaudividniforebmungolehtsinoitacfiiceps .atadxatSRIotdehctamSDLSNehtmorfemocatadllA.level etavirP cilbuP tiforP-roF )3( )2( )1( 5385220. 5402220. ***5535270. ffotuC evobA ) 3637720.( ) 5747620.( )3090510.( 002 002 002 snoitavresbO 55

TableA.3: AnalysisVariableDescriptions Notes: Thistabledescribesthemainanalysisvariables.Thefirstcolumnpresentsthevariablename. Thesecondcolumnpresentsadescriptionsofthevariable. Thethirdcolumnpresentsthesourceof thevariable.Allloan,grant,andearningamountsrefertoannualamounts. Variable Description Source Federal Loans Total federal Direct and FFEL loans. NSLDS Non-Need Based Total unsubsidized federal Direct and Federal Loans FFEL loans. NSLDS Need Based Total subsidized federal Direct and Federal Loans FFEL loans. NSLDS Parent Loans Total federal PLUS loans. NSLDS Pell Grants Total Pell Grants. NSLDS Number of days from turning 24 in the Assignment calendar year enrolled. NSLDS Mortgage Presence of mortgage interest. 1098 Information Returns Wages Labor earnings. W-2 Information Returns Works Presence of labor earnings. W-2 Information Returns Enrollment Indicator of college enrollment. 1098-T Information Returns Spouse Indicator of whether married. Form 1040 Savings Presence of interest or dividend income. 1099 Information Returns Children Indicator of any children. Social Security Card Applications 56

TableA.4: EffectofLimitIncreaseonParentBorrowing Notes: ThistableshowsregressiondiscontinuityestimatesonfederalloansandfederalparentPLUSloans.Eachvariableisdenotedabovetheestimates.Thefirstcolumn showstotalstudentborrowing. Thecolumninthemiddleshowstotalhouseholdborrowing including parent borrowing. Specifications include a quadratic spline of the assignmentvariable,whichisthenumberofdaysfromturning24inthecalendaryear ofthediscontinuity.AlldatacomefromtheNSLDSmatchedtoIRStaxdata.*p<.1, **p<.05,***p<.01. Federal Loans Total Minus Par. PLUS Loans (1) (2) (3) Above Cutoff 1,892.918*** 1,534.904*** -358.0144*** (44.110813) (52.33988) (31.11639) Observations 464,008 464,008 464,008 57

sreworroBeloHtunoDgnidulcnIstluseRpihsrenwoemoH :5.AelbaT eloh tunod eht gnidulcni ,sraey retal dna ytiunitnocsid eht fo raey eht ni setamitse ytiunitnocsid noisserger swohs elbat sihT :setoN morfsyadforebmunehtsihcihw,elbairavtnemngissaehtfoenilpscitardauqaedulcnisnoitacfiicepS .sisylananiamehtnidedulcxe ehtmorfemocatadllA .levelffotucmorfyadehttaderetsulcerasrorredradnatS .ytiunitnocsidehtforaeyradnelacehtni42gninrut .10.<p***,50.<p**,1.<p*.atadxatSRIotdehctamSDLSN )6( )5( )4( )3( )2( )1( retfA sraeY eviF retfA sraeY ruoF retfA sraeY eerhT retfA sraeY owT retfA raeY fo raeY nI ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD **362900. ***6231210. ***917310. ***4054110. ***5412700. ***4220500. ffotuC evobA )4873000.( )2035000.( )9196000.( )1795000.( )6732000.( )4911000.( 683,573 868,314 052,454 812,494 812,494 812,494 snoitavresbO 58

enilpSraeniLotstluseRpihsrenwoemoHfossentsuboR :6.AelbaT morfyadehttaderetsulcerasrorredradnatS.enilpscitardauqanahtrehtarraenilagnisu,ytiunitnocsidehtforaeyehtnistluserswohsnmulocpotehT:setoN .10.<p***,50.<p**,1.<p*.atadxatSRIotdehctamSDLSNehtmorfemocatadllA.levelffotuc )6( )5( )4( )3( )2( )1( retfA sraeY eviF retfA sraeY ruoF retfA sraeY eerhT retfA sraeY owT retfA raeY fo raeY nI ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD 3593500.0 5125500.0 5431400.0 **2998500.0 **145500.0 ***007400.0 ffotuC evobA )5579300.0( )8285300.0( )6492300.0( )6176200.0( )013200.0( )706100.0( 908,672 030,503 698,433 154,463 154,463 154,463 snoitavresbO 59

TableA.7: HumanCapitalandSavingsOvertheNearTerm Notes: Thistablepresentsnear-termhumancapitalandsavingsoutcomesThedependentvariableislistedabove each specification. The first column presents results in the year of the discontinuity, and the second column presentsresultsoneyearlater. Specificationsincludeaquadraticsplineoftheassignmentvariable,whichisthe numberofdaysfromturning24inthecalendaryearofthediscontinuity. Standarderrorsareclusteredattheday fromcutofflevel.AlldatacomefromtheNSLDSmatchedtoIRStaxdata.*p<.1,**p<.05,***p<.01. (1) (2) In Year of Year After Discontinuity Discontinuity Wages Above Cutoff -240.2872* -92.09363 (130.9886) (178.074) Works Above Cutoff -0.0027539 0.001999 (0.0030782) (0.002867) Enroll Above Cutoff -0.002054 0.002841 (0.0044338) (0.00549) Enroll at Least Half Time Above Cutoff -0.0015745 0.006798 (0.0049517) (0.0054893) Savings Above Cutoff 0.0248975*** 0.007189 (0.0048689) (0.00492) Amount of Savings Above Cutoff -0.9384397 0.240176 (1.928757) (1.966781) Observations 464,008 464,008 60

enilpSraeniLotssentsuboRsgnivaSdnalatipaCnamuH :8.AelbaT ytiunitnocsid noisserger swohs elbat ehT .stluser emoctuo tekram robal niam eht rof snoitacfiiceps evitanretla stneserp elbat sihT :setoN nielbairavtnednepedehT .ytiunitnocsidehtretfasraeyevfidnaytiunitnocsidehtretfasraeyeerht,ytiunitnocsidehtforaeyehtnisetamitse ehT.sgninraeynastroperlaudividninarehtehwgnitonedrotacidninasilenapelddimehtnielbairavtnednepedehT.sgninraesilenappoteht eht fo enilps raenil a edulcni snoitacfiicepS .emocni dnedivid ro tseretni sah reworrob a rehtehw si lenap mottob eht ni elbairav tnedneped ehttaderetsulcerasrorredradnatS.ytiunitnocsidehtforaeyradnelacehtni42gninrutmorfsyadforebmunehtsihcihw,elbairavtnemngissa .10.<p***,50.<p**,1.<p*.atadxatSRIotdehctamSDLSNehtmorfemocatadllA.levelffotucmorfyad segaW )3( )2( )1( retfA sraeY eviF retfA sraeY eerhT fo raeY nI ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD 3716.103- 311561.3 ***5700.223ffotuC evobA )4959.252( )9775.202( )78782.68( 908,672 698,433 154,463 snoitavresbO kroW )3( )2( )1( retfA sraeY eviF retfA sraeY eerhT fo raeY nI ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD 1378100.0 7716000.0 **7462400.0ffotuC evobA )7834200.( )690200.( )8221200.( 908,672 698,433 154,463 snoitavresbO sgnivaS )3( )2( )1( retfA sraeY eviF retfA sraeY eerhT fo raeY nI ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD 3670400.0- 9562200.0- ***2415810.0 ffotuC evobA )6916300.( ) 7413300.( )1870300.( 908,672 698,433 154,463 snoitavresbO 61

setamitsEnoitelpmoC :9.AelbaT gnitonedrotacidninasielbairavtnednepedehT.sraeyretaldnaytiunitnocsidehtforaeyehtnisetamitseytiunitnocsidnoissergerswohselbatsihT:setoN gninrutmorfsyadforebmunehtsihcihw,elbairavtnemngissaehtfoenilpscitardauqaedulcnisnoitacfiicepS .eergedasetelpmoclaudividninarehtehw xatSRIotdehctamSDLSNehtmorfemocatadllA.levelffotucmorfyadehttaderetsulcerasrorredradnatS.ytiunitnocsidehtforaeyradnelacehtni42 .10.<p***,50.<p**,1.<p*.atad )6( )5( )4( )3( )2( )1( retfA sraeY eviF retfA sraeY ruoF retfA sraeY eerhT retfA sraeY owT retfA raeY fo raeY nI ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD 8760600.0 7216600.0 8330800.0 7735600.0 8651200.0 1508200.0 ffotuC evobA )1083600.0( )8800600.0( )4869500.0( )8677500.0( )4428500.0( )5563500.0( 644,253 815,883 874,624 800,464 800,464 800,464 snoitavresbO 0>CFE CFE oreZ retfA sraeY eviF retfA sraeY eerhT fo raeY retfA sraeY eviF retfA sraeY eerhT fo raeY ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD ytiunitnocsiD 2852600.0 4321900.0 3124900.0 2514210.0 9587110.0 6808410.0ffotuC evobA )1813700.0( )7328600.0( )1267600.0( )6691810.0( )887510.0( )3368210.0( 013,611 013,611 013,611 989,38 989,38 989,38 snoitavresbO 62

TableA.10: HumanCapitalbyEFC Notes: Thistableshowsregressiondiscontinuityestimatesintheyearofthediscontinuity,threeyears afterthediscontinuityandfiveyearsafterthediscontinuity,splitbyzeroEFC.Thedependentvariablein thefirstthreerowsisearnings.Thedependentvariableinthesecondthreerowsisanindicatordenoting whetheranindividualreportsanyearnings. Specificationsincludeaquadraticsplineoftheassignment variable,whichisthenumberofdaysfromturning24inthecalendaryearofthediscontinuity.Standard errorsareclusteredatthedayfromcutofflevel.AlldatacomefromtheNSLDSmatchedtoIRStaxdata. *p<.1,**p<.05,***p<.01. Zero Positive EFC (1) (2) Wages Year 0 373.3942 -191.8393 (91.0224) ( 157.593) 3 572.1077 -246.4874 (847.8236) (317.4298) 5 1138.049 -567.1655 (847.0266) (439.1978) Work Year 0 .0100955 -.0053298 (.0081865) (.0038368) 3 -.0011522 -.0000513 (.0080169) (.0035732) 5 .0053052 -.0022812 (.0110249) (.0043729) Observations 90,690 302,837 63

TableA.11: MainHomeownershipResultsbySector Notes: Thistablepresentsthemainresults,byschooltype. Thefirstcolumnpresentsresultsforpublicschools granting four-year degrees, the second column presents results for private nonprofit schools granting four-year degrees, and the third column presents results for nonprofit schools granting two year degrees, Specifications includeaquadraticsplineoftheassignmentvariable,whichisthenumberofdaysfromturning24inthecalendar year of the discontinuity. Standard errors are clustered at the day from cutoff level. All data come from the NSLDSmatchedtoIRStaxdata.*p<.1,**p<.05,***p<.01. Public Private Comm. College (1) (2) (3) Mortgage Year 0 .0051635* .0013525 .0161729 (.0027335) (.0056301) (.0118298) 1 .0054716 .008545 .0211923 (.0037503) (.0073645) (.0144806) 2 .0072544 .0076952 .0258244 (.0045175) (.008854) (.0170883) 3 .0103724* .0087086 .0315956 (.0056664) (.0101194) (.0203247) 4 .0117386* -.0005293 .0354505 (0.0062921) (.0118479) (.02282453) 5 .0095257 .0051272 .0182377 (.0070388) (.0127207) (.0272335) Observations 337,745 94,157 32,106 64

TableA.12: EffectsofLimitIncreaseonLoansandGrantsbySector Notes: This table presents limit increase results by school type. The first column presents results for public schools granting four-year degrees, the second column presents results for privatenonprofitschoolsgrantingfour-yeardegrees,andthethirdcolumnpresentsresultsfor nonprofit schools granting two-year degrees, Specifications include a quadratic spline of the assignmentvariable, whichisthenumberofdaysfromturning24inthecalendaryearofthe discontinuity.Standarderrorsareclusteredatthedayfromcutofflevel.Alldatacomefromthe NSLDSmatchedtoIRStaxdata.*p<.1,**p<.05,***p<.01. Public Private Comm. College (1) (2) (3) Total Loans 1,866.153*** 2,365.588*** 1,010.127*** (49.12869) (99.82655) (123.0574) Total Grants 1,427.308*** 1,398.384*** 905.9641*** (35.48191) (52.55398) (88.82216) Observations 337,745 94,157 32,106 65

TableA.13: FamilyFormationOutcomesRobustness Notes:Thistablepresentsalternativespecificationsforthemainfamilyformationresults.Thetableshowsregression discontinuityestimatesintheyearofthediscontinuity, threeyearsaftertheyearofthediscontinuityandfiveyears afterthediscontinuity. Thedependentvariableinthetoppanelisanindicatorofwhetheraborrowerismarried. The dependentvariableinthesecondcolumnisanindicatordenotingwhetheranindividualhashadanychildrenbythat year.Specificationsincludealinearsplineoftheassignmentvariable,whichisthenumberofdaysfromturning24in thecalendaryearofthediscontinuity. Standarderrorsareclusteredatthedayfromcutofflevel. Alldatacomefrom theNSLDSmatchedtoIRStaxdata.*p<.1,**p<.05,***p<.01. Marriage (1) (2) (3) In Year of Three Years After Five Years After Discontinuity Discontinuity Discontinuity Above Cutoff -0.0019367 0.006721* 0.0098406** (.0019192) (.003609) (.0043012) Observations 364,451 334,896 276,809 Children (1) (2) (3) In Year of Three Years After Five Years After Discontinuity Discontinuity Discontinuity Above Cutoff 0.00024714 0.00443186* 0.00841002** (.00099316) (.00262697) (.00403502) Observations 364,451 334,896 276,809 66