Personal Finance Education Mandatesand Student Loan Repayment∗

Daniel Mangrum†

January 21, 2021

Abstract

Many states in theU.S. require students to complete personal finance educationin order to graduate high school. I investigate whether personal financial liter-acy (PFL) requirements for high school students improve federal student loanoutcomes after college. In contrast to previous studies, I develop a novel iden-tification strategy using university-level repayment outcomes which improvesthe assignment of mandate status and separates the effect on borrowing fromthe effect on repayment. I find that PFL mandates have varying impacts acrossbroad student types. I find that only higher income students adjust their useof student loan debt, reducing extensive borrowing by around 8%. However,first generation and low income borrowers who were bound by mandates aremore likely to pay down balances during the first year of repayment. Thisimprovement is not the result of smaller loan balances, but instead may be dueto improved understanding of the terms and rules governing federal studentloans. These improvements in repayment are likely to reduce the amount offederal student loans that are ultimately forgiven or defaulted.

Keywords: financial literacy, student loans, high school curriculum, postsecondary finance.JEL: D14, H41, I22, I28, I26, J24.

∗I am grateful to Andrea Moro, Kitt Carpenter, Andrew Dustan, Lesley J. Turner, Brent Evans,Carly Urban, Andrew Goodman-Bacon, Michelle Marcus, Paul Niekamp, Nicolas Mäder, and TamBui for comments as well as discussants and seminar participants at the Missouri Valley EconomicAssociation Annual Conference, Southern Economic Association Annual Conference, Association forEducation Finance and Policy Annual Conference, the Washington Center for Equitable Growth, theUniversity of Memphis, Western Illinois University, the University of Georgia, the Federal ReserveBank of New York, CNA Corporation, the Urban Institute, the Bureau of Labor Statistics, and MiddleTennessee State University. This work was supported by the Kirk Dornbush Dissertation Fellowshipand theWashingtonCenter for EquitableGrowth. The views expressed herein are those of the authorsand do not represent those of the Federal Reserve Bank of New York or the Federal Reserve System.

†Federal Reserve Bank of New York, 33 Liberty Street, New York, NY 10045;

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1 Introduction

In the United States, high school students are increasingly tasked with makingconsequential human capital investment decisions with limited information sets.Some of these decisions include whether to attend college, which college to at-tend, and how to finance postsecondary education. Perhaps as a result, 47% ofAmericans with student loan debt say they would have accepted fewer federal aiddollars if they could make the choice again, and over half say they’ve had diffi-culties making monthly payments (Consumer Reports, 2016). These difficultiescan be compounded for first generation students who often do not have access tomentors with first-hand experience in postsecondary education. These students areless likely to apply for admission to selective universities, are less likely to retakestandardized tests, and are more likely to under-invest in postsecondary education(Hoxby and Turner, 2015; Goodman, Gurantz, and Smith, 2020; Avery and Turner,2012).

In this paper, I study an intervention that might improve outcomes for highschool students making human capital investment decisions: mandated personalfinancial literacy (PFL) coursework. Specifically, I investigate whether PFL educa-tion during high school improves postsecondary finance outcomes by providingstudents with additional information at the critical time these decisions are made.Between 1993 and 2014, 23 states adjusted high school graduation requirements toinclude topics covering personal financial literacy (Stoddard and Urban, 2020). Themain objective for the focus on PFL is to increase the overall financial literacy of thestate population, but many of the state standards include topics discussing post-secondary education and career research. Since enrollment in these courses oftencoincides with the timing of the federal financial aid application process, requiringpersonal finance education in high school can operate as a just-in-time informationintervention to improve postsecondary finance outcomes.

This paper marks a methodological improvement on previous studies that as-sign a student’s high school state (and thus mandate status) using either the stateof residence or the state of birth (Cole et al., 2016; Bernheim et al., 2001). In-stead, I employ a novel identification strategy which exploits plausibly exogenousvariation in university-level exposure to state mandates. When states adjust highschool graduation requirements to include PFL topics, universities become increas-ingly populated by students who were exposed to this course content during highschool. Universities vary in their exposure to state standards because their studentbodies have different shares of incoming students from adopting states. I show that,under the necessary assumptions, this identification strategy consistently estimatesthe borrower level effect of PFL mandates on student loan outcomes.

As for borrower outcomes, I testwhetherPFLmandates affect the level of studentdebt upon first entering repayment. Previous work examines either the initial use

daniel.mangrum@ny.frb.org

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of federal student loans (Stoddard and Urban, 2020) or total outstanding studentloan balances (Brown et al., 2016), the latter of which is affected total borrowing,accumulated interest, and pace of repayment. In contrast, I investigate how PFLmandates affect total student borrowing at the point a student enters repaymentwhich is independent of the potentially endogenous pace of repayment. Thismeasure more accurately reflects undergraduate student borrowing and separatesborrowing fromrepayment. I find significant heterogeneity in the effect ofmandateson borrowing. While higher income students reduce federal borrowing by around8%, first generation, lower income, andmiddle income students do not significantlyadjust borrowing. This heterogeneity is likely due to high income students havingmore alternative borrowing sources than lower income students in the form offamily wealth and private sources. Additionally, students bunching at federal loanlimits reduces the ability to adjust borrowing.

Next, this is the first paper to estimate the impact of PFL mandates specificallyon student loan repayment. To this end, I study two measures of federal studentloan repayment progress that vary in severity and sensitivity. The first measure,loan default, is a more adverse and relatively rare outcome yet is most often usedas the benchmark for repayment. However, due to deferment, forbearance, andincome-driven repayment (IDR) plans, borrowers often can avoid default while stillmaking no progress toward repaying loans. As such, I focus on a more sensitivemeasure of student loan repayment, the repayment rate, which measures whethera borrower’s loan principal is declining. I find no significant impact of mandateson student loan default likely because default is becoming easier to avoid throughdeferment, forbearance, and income based repayment (Herbst, 2020). However, Ido find that mandates improve student loan repayment. The effect is largest forstudents at public universities and especially for first generation students and forstudents from households earning less than $30,000 per year. The estimates suggesta 5% increase in the probability these students are able to pay down some of theirbalance during the first year of repayment. I also present evidence that borrowersachieving this benchmark are less likely to have a balance remaining upon reachingtheir forgiveness date.

Lastly, I investigate the primary channel by which information might improvestudent loan outcomes. Using a nationally representative sample of college stu-dents, I investigate whether students bound by personal finance mandates arebetter able to answer financial literacy questions and questions pertaining to thefederal student loan system. I find no significant improvement in a student’s abilityto answer financial literacy questions, but students are slightly better able to an-swer questions surrounding the terms and regulations governing federal studentloans. This result is consistent with evidence from the literature that find informa-tion interventions for vulnerable populations can improve postsecondary outcomes(Bettinger et al., 2012; Castleman and Goodman, 2018; Barr et al., 2016; Bettingerand Evans, 2019; Gurantz et al., 2020).

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2 Background

2.1 Federal Financial Aid

In order to qualify for federal student loans, students must complete a FreeApplication for Federal Student Aid (FAFSA) which collects details about studentsand their families including incomeandasset information. While federal subsidizedloans are means-tested based on information from the FAFSA, unsubsidized loansare available to any student.1 Students also face limits on federal borrowing basedon the loan type, year of schooling, university Cost of Attendance (COA), and otherfinancial aid received.

Evidence from the literature has largely concluded that access to financial aidincreases access to higher education for low income students (Dynarski, 2003) andmore recent evidence suggests increased student loan borrowing causes highergrades and more completed credits for community college students (Marx andTurner, 2019b). Despite the benefits, studies have been critical of the burdensomebureaucracy and complicated process for applying for and receiving financial aid(Dynarski and Scott-Clayton, 2006; Novak and McKinney, 2011; Bettinger, Long,Oreopoulos, and Sanbonmatsu, 2012; Dynarski and Scott-Clayton, 2013; Scott-Clayton, 2015).2 Critics often argue that the complicated applicationprocess and themultitude of choice options tend to reduce the receipt of aid for students that wouldotherwise be eligible and encourages students to opt into default options (Kofoed,2017; Marx and Turner, 2019a). Even for students that successfully navigate theapplication stage, complexities surrounding the number and type of repaymentplans can lead to issues during repayment (Cox, Kreisman, and Dynarski, 2020;Abraham, Filiz-Ozbay, Ozbay, and Turner, 2020). The evidence presented in thispaper is consistentwith the literature that finds improvements in outcomes throughreducing the barriers to federal financial aid access.

A few recent studies find that interventions that provide students with moreinformation about college applications and federal financial aid improve outcomesfor students from disadvantaged backgrounds. Bettinger, Long, Oreopoulos, andSanbonmatsu (2012) show that providing low income families with assistance com-pleting the FAFSA can dramatically increase the probability of applying for federalaid and increase college enrollment and persistence. Barr, Bird, and Castleman(2016) find that providing information to community college students about federalstudent loan options can shift borrowers away from higher cost financing which islargely driven by studentswith lower levels of financial literacy and higher debt bal-ances. Gurantz, Pender,Mabel, Larson, andBettinger (2020) find that virtual collegecounseling that targets low and middle income students increased the probability

1Subsidized loans are loans in which interest does not accrue while the student is in school whileunsubsidized loans begin accruing interest after dispersement.

2Castleman, Schwartz, and Baum (2015) summarizes several studies that test interventions de-signed to improve the decision making process in investing in higher education.

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students chose to attend a college with a high graduation rate. Additionally, Castle-man and Goodman (2018) find that college counseling can increase low incomestudent enrollment and persistence in less expensive four-year public universitieswith higher graduation rates. Bettinger and Evans (2019) also find that peer advis-ing from recent college graduates to high school students can increase enrollment intwo-year colleges for low income andHispanic studentswithout reducing four-yearenrollment. Lastly, informational interventions that increase enrollment in income-driven repayment (IDR) plans may also improve federal student loan repayment.Herbst (2020) finds that enrollment in IDR plans improves repayment and reducesdelinquencies resulting in a faster pace or student loan repayment.

2.2 Personal Finance Education

One large scale intervention that might improve postsecondary outcomes fordisadvantaged students is the addition of personal financial literacy (PFL) educationduring high school. The first string of literature investigates an earlier wave offinancial literacy education which occurred between 1957 and 1982. AlthoughBernheim et al. (2001) finds some correlational evidence that required financialliteracy courses during this wave improve financial outcomes, Cole et al. (2016)finds these results are not robust to the inclusion of state and year fixed effects.Cole et al. (2016) conclude that students who were bound by this earlier wave ofmandates had no better financial outcomes than students who were not mandated.On the other hand, Brown et al. (2016) studies a more recent wave of personalfinance education mandates and finds improvements in credit outcomes for youngborrowers. Theyfind that themandatedPFLcourseworkbinding since 1998 reducesthe amount of delinquent debt held by young adults. They also find the effectgrows as mandates mature suggesting either implementation lags on the part ofschools or improvements in teaching efficiency over time. Harvey (2019) findsthat young people bound by mandates are less likely to use alternative financialserviceswhich typically carryveryhigh interest rateswithhigh rates of delinquency.Urban, Schmeiser, Collins, and Brown (2018) compare credit report data acrossmandated and non-mandated young people and find that those who were boundby personal finance education mandates during high school have fewer delinquentcredit accounts and higher credit scores.

This paper is most closely related to Stoddard and Urban (2020) which studieshow PFL mandates affect the receipt of federal student aid for first year college stu-dents. Using a difference-in-differences design with several waves of the NationalPostsecondary Study of Student Aid (NPSAS), they find that mandated collegefreshmen are more likely to complete the FAFSA, more likely to borrow from fed-eral sources, more likely to receive grants or scholarships, borrow fewer privateloans, and are less likely to carry a credit card balance. They also find that theimpact on extensive borrowing of federal loan dollars and the lower likelihood ofcredit card borrowing is larger for low income students and these students are also

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less likely to work while enrolled in college.I extend this literature in several key dimensions. First, I introduce a novel

identification strategy which relies on university level student loan outcomes toproxy borrower level outcomes. In contrast to many previous studies, this strategydoes not assume the borrowers’ high school graduation state is the state of residencethus reducing potential attenuation bias. Instead, I follow cohorts of students fromhigh school, to college, and through repayment. I also explore whether the effect ofPFL mandates differs depending on demographics of the university student bodysuch as income and first-generation status. Next, I present additional evidenceto support the findings in Stoddard and Urban (2020) showing that high schoolstudents who were bound by PFL mandates did not alter their choice to attendcollege or the selection of post-secondary institution. While Stoddard and Urban(2020) studies the effect of mandates on first year borrowing and Brown et al. (2016)explores the effect on total outstanding student loan balances throughout youngadulthood, I focus on student loan balances upon entering repayment which allowsme to separate the effect of debt accumulation versus debt repayment. In studyingrepayment, I focus on two primary outcomes measuring student loan repaymentsuccess. The first, student loan default, is most commonly studied in the literature,is used to regulate universities, but can often be manipulated or avoided (CITE).3On the other hand, I study a measure of short-term repayment success that is moresensitive and is predictive of long-term repayment success. Lastly, I investigatewhich information channel is primarily responsible for improvements in outcomes.

2.3 Mechanisms

To better understand how mandated personal finance education can influencestudent loan repayment after college, consider the case of two otherwise identicalhigh school students in which one student (the treated student) is required to beexposed to personal finance education during high school (as in Figure 1) andthe second student (the untreated student) is not. There are many avenues forthe intervention to affect repayment outcomes since exposure to personal financeeducation occurs during high school (C) and student loan repayment does not beginuntil after college (C + 5). The three categories of course content most likely todirectly or indirectly affect student loan repayment are topics on financial literacy,financial aid, and career research.

First, since the goal of most PFL mandates is to improve financial literacy, thestandards typically focus on topics such as interest, inflation, risk tolerance, insur-ance, budgeting, and investing.4 As a result, students bound by PFLmandates maybe better at managing money, be more likely to understand the risks of borrowing,and be more likely to make on time loan payments. The state standards for many

3https://www.gao.gov/assets/700/691520.pdf4Figure A.5 shows a word cloud of the text of all PFL state standards.

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Figure 1: Example Timeline for Personal Financial Literacy Education Interventionthrough to Student Loan Repayment

• • • • • • •C C + 1 C + 2 C + 3 C + 4 C + 5 C + 6

High School

PersonalFinance+

College Grace Repayment

courses require students to “examine ways to avoid and eliminate credit card debt”(Texas5), “design afinancial plan for earning, spending, saving, and investing” (Mis-souri6), and “evaluate the different aspects of personal finance including careers,savings and investing tools, and different forms of income generation” (Michigan7).However, most studies that evaluate small scale financial literacy interventionsfind little to no improvement in financial literacy and most improvements depre-ciate quickly (Huston, 2010; Fernandes, Lynch Jr, and Netemeyer, 2014). On theother hand, some evidence shows that financial literacy interventions during highschool can improvemore objectivemeasures of financial health such as credit scores(Brown, Grigsby, van der Klaauw, Wen, and Zafar, 2016; Urban, Schmeiser, Collins,and Brown, 2018).

Second, the required coursework may help students navigate the federal finan-cial aid system. In many states, the PFL standards require students to research howtofinance postsecondary education. For example, students inOregonmust researchthe costs and benefits of using loans to finance higher education8 and students inTexas should “research and evaluate various scholarship opportunities.”9 Somestates require students to practice applying for federal financial aid and researchthe differences in various aid types. Tennessee’s state standards require studentsto research both positive and negative aspects of borrowing federal student loans10while Utah students must “utilize the FAFSA4caster to explore the FAFSA pro-cess.”11 Since this material is taught at roughly the same time students are applyingto college and applying for federal aid, this information is more likely to affectpost-secondary decision-making. Additionally, students may be more aware ofincome-driven repayment plans which can lead to better repayment outcomes aftercollege (Herbst, 2020).

5https://web.archive.org/web/20111107152521/http://ritter.tea.state.tx.us/rules/tac/chater118/ch118a.html

6https://dese.mo.gov/sites/default/files/personal_finance_competencies.pdf7https://www.michigan.gov/documents/mde/SS_COMBINED_August_2015_496557_7.pdf8https://www.ode.state.or.us/teachlearn/subjects/socialscience/standards/oregon-social-sci

ences-academic-content-standards.pdf9https://web.archive.org/web/20111107152521/http://ritter.tea.state.tx.us/rules/tac/chap

ter118/ch118a.html10https://www.tn.gov/content/dam/tn/education/ccte/cte/cte_std_personal_finance.pdf11https://www.schools.utah.gov/file/6348311c-77c7-4fbd-87e7-ba3484bddb6e

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Third, many PFL course requirements direct students to research various ca-reers, colleges, and majors. Students bound by various state mandates are requiredto “explore potential careers and the steps needed to achieve them” (Arkansas12) orto “identify a career goal and develop a plan and timetable for achieving it, includ-ing educational/training requirements, costs, and possible debt” (New Jersey13).These activities during the personal finance coursework might cause students tobe more aware of various career paths and education requirements which mightbetter prepare students for success in college.

3 Data

I use the College Scorecard database to monitor changes in federal student loanoutcomes across university cohorts. The College Scorecard was developed duringthe Obama Administration and debuted in 2015 as a website tool to provide moreinformation to potential college students. The Department of Education providesthe underlying university-level data dating back to the 1996-1997 academic year andupdates the data frequently. The federal student loan variables are constructed us-ing the administrativeNational Student LoanData System (NSLDS)which containsrecords on the universe of federal aid recipients.

For the analysis, I restrict focus to four-year baccalaureate universities.14 I alsoremove universities that aggregate student loan outcomes across multiple branchcampuses and universities that do not receive federal financial aid.15 In order toconstruct a balanced panel, I remove universities that either enter or exit the sampleduring the sample window.16 The resulting sample contains 1,386 universitiesacross 50 states and the District of Columbia of which 450 are public universities

12http://www.arkansased.gov/public/userfiles/Learning_Services/Curriculum%20and%20Instruction/Frameworks/Personal_Finance/Economics-aligned-to-PF-Standards.pdf

13https://www.state.nj.us/education/cccs/2014/career/91.pdf14Although the sample of two-year university students merits attention, the identification strategy

described in the next section relies on following students that transition from high school into collegewithin 12 months of graduating high school. As such, I restrict the sample to four-year universitiessince high school graduates are more likely to transition immediately to a four-year university than atwo-year university.

15This restriction is necessary due to the nature of the identification strategy discussedin the next section. When a university system aggregates outcome measures across multi-ple branches, the identifying variation on the right-hand-side of the estimating equation isaggregated at a smaller granularity than the outcome measure on the left-hand-side. Thereasoning behind the varying level of aggregation is discussed in footnote 17 of Using Fed-eral Data to Measure and Improve the Performance of U.S. Institutions of Higher Education found athttps://collegescorecard.ed.gov/assets/UsingFederalDataToMeasureAndImprovePerformance.pdf.

16This can occur due to a university opening or closing or a university opting into or losing accessto federal aid. This restriction helps to alleviate the concern of selection into or out of the sample.Universities may lose access to federal aid as a result of poor student loan repayment or choose tobegin accepting federal aid as a result of unobservables that change over time. Looney, Yannelis, et al.(2019) notes that the majority of the variation in cohort defaults over time stem from entry into and

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and 936 are private universities.17The first outcome of interest is the total student loan debt upon a borrower’s

entry into repayment. The Scorecard includes the 10th, 25th, 50th, 75th, and 90thpercentile of federal student loan debt upon entering repayment for each universityrepayment cohort. Further, median student loan debt is reported separately forfirst generation students (students whose parents did not have a college degreeupon college entry), low income students (students with household income lessthat $30,000 upon college entry),middle income students (studentswith householdincomebetween $30,000 and $75,000 upon college entry), andhigh income students(students with household income above $75,000 upon college entry).18

Next, the Scorecard produces two measures student loan repayment for eachuniversity’s repayment cohort. The first is the two-year cohort default rate whichis calculated by dividing the total number of students who have defaulted ontheir student loans within two years of entering repayment by the total number ofborrowers in the repayment cohort.19 Defaultwithin thefirst twoyears of repaymentis a relatively rare but adverse event which borrowers are increasingly able to avoidthrough forbearance, deferment, or enrolling in an income-driven repayment (IDR)plan. As a result, this outcome is less sensitive to change.20 On the other hand, theScorecard also constructs the one-year repayment rate which calculates the shareof the repayment cohort who are not in negative amortization at the end of the firstyear of repayment. Since borrowers can enroll in deferment, forbearance, or IDR, itis possible for borrowers to not enter default yet have a balance at the end of theirfirst year of repayment which is larger than their original balance. As a result, theone-year repayment rate is a more sensitive measure of student loan repaymentprogress since it calculates the share of a repayment cohort who have a smallerbalance after one year of repayment.21 Similar to the measures of median studentloan debt, the Scorecard also reports the one-year repayment rate separately for firstgeneration, low income, middle income, and high income students.

Table 1 reports summary statistics for the sample of universities for the mainoutcome variables. I present the means and standard deviations weighted by the

out of the student loan market. Since the focus of the paper is borrower level impacts and not universitylevel impacts, the results should not be driven by university level factors.

17Figure A.4 plots the locations of the universities in the sample.18The College Scorecard uses nominal dollars to determine these bins. As a result, students with

similar household incomes in real terms might be shifted into higher income bins over time due toinflation.

19A borrower enters default after 270 consecutive days without making a payment. Default forstudents loans is atypical compared to other consumer debt. Upon default, there is no repossessionof assets since the loans are unsecured. Rather, the federal government levies fines and allows loanservices to garnish wages and tax refunds to collect outstanding debts.

20Note the smaller standard deviation relative to the mean for default rate relative to repaymentrate in Table 1.

21I show in Table 5 that achieving this benchmark is predictive of long term success in payingdown student loans and avoiding default.

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number of borrowers used in constructing each university outcome to be repre-sentative of the population of student loan borrowers. Generally, student loandebt is larger at private universities than at public universities, however repaymentoutcomes tend to be better at private universities than public universities (lowerdefault rates and higher repayment rates). One important exception to this trend isfor first generation and low income students who have higher repayment rates atpublic universities than at private universities. Over the sample, the default rate isrelatively low at 4.2% while the repayment rate shows that around 60% of studentloan borrowers are able to pay down at least some of their balance after one year ofrepayment.

In addition to theCollege Scorecard, I use the national rollout of personal financeeducation mandates since 1990 from Stoddard and Urban (2020) which is detailedin Table 2. Stoddard and Urban (2020) improve on the definition of state mandatesfrom Brown et al. (2016) by more systematically defining the effective year of PFLmandate using the first high school graduating class that was bound by a mandate.PFL standards are most often included in other required courses such as SocialStudies, Economics, and Math. However, several of the more recently adoptingstates have started requiring students to complete a standalone course in personalfinance.

Lastly, I use data from the Integrated Postsecondary Education Data System(IPEDS) which includes biannual counts of the incoming cohort of students by pre-vious state of residence for each university. Between 1986 and 1994, these data werecollected every two years from each university and after 1994, universities couldvoluntarily provide these data to IPEDS in odd years, but were required to submitcounts in even numbered years. I use counts of first-time degree seeking studentswho graduated high school within 12 months of entering college. I replace missingstudent counts in odd years with linearly interpolated values from neighboringeven years.22

Additional information on these data sources along with supplemental datasources are detailed in Appendix A.2.

22In Appendix A.4.3, I instrument student counts using a combination of fixed effects, observablepolicy changes, and linear and quadratic trends to replace missing values with estimated values.

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Table 1: Descriptive Statistics

All Universities Public Universities Private Universities(n=1,386) (n= 450) (n= 936)

Outcome Variable Mean SD Mean SD Mean SD

Student Loan Debt10th 2,594.5 (664.3) 2,480.3 (542.8) 2,847.0 (979.8)25th 4,525.7 (1,669.1) 4,181.4 (1,224.7) 5,128.1 (2,521.2)MedianOverall 10,373.3 (3,824.4) 9,516.4 (3,083.5) 12,074.4 (5,067.8)First Gen 9,947.5 (3,804.9) 9,288.9 (3,121.0) 11,470.9 (5,195.6)Low Income 9,805.0 (3,598.7) 9,289.7 (2,860.9) 11,552.1 (5,019.7)Middle Income 10,943.5 (4,101.0) 9,911.5 (3,345.1) 12,174.0 (5,846.5)High Income 10,835.9 (4,134.0) 9,602.7 (3,451.4) 11,831.0 (5,788.6)

75th 18,584.8 (4,487.8) 18,172.4 (4,092.3) 19,369.9 (5,683.1)90th 26,111.9 (5,655.3) 25,959.9 (5,188.9) 25,905.9 (7,374.0)

Default Rate 0.042 (0.032) 0.046 (0.031) 0.036 (0.034)Repayment RateOverall 0.594 (0.170) 0.593 (0.149) 0.595 (0.199)First Gen 0.536 (0.165) 0.551 (0.147) 0.512 (0.188)Low Income 0.458 (0.170) 0.478 (0.151) 0.423 (0.194)Middle Income 0.631 (0.148) 0.630 (0.136) 0.632 (0.166)High Income 0.749 (0.114) 0.730 (0.107) 0.777 (0.117)

Means and standard deviations for the main outcome variables are presented above for the fullsample and separately by institution control. Moments are weighted by the number of borrowersused to compute each outcome in order to be representative of the population of student borrowers.Student loan debt amounts are reported upon borrower entry into repayment. Median student loandebt is reported for the full repayment cohort and separately for first generation students (studentswhose parents did not have a college degree) and for students by household income bins. Lowincome is defined as students with family income less than 30,000 upon entering college. Middleincome is defined as between 30,000 and 75,000 and high income is defined as above 75,000. Thedefault rate is the two-year cohort default rate from FY1995 to FY2013. The one year repaymentrate is reported for the full repayment cohort and separately for first generation students (studentswhose parents did not have a college degree) and for students by household income bins.

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Table 2: Implementation of Personal Financial Literacy (PFL) Mandates Since 1990

State Coursework First Cohort Bound

New Hampshire Incorporated (Economics) 1993New York Incorporated (Economics) 1996Michigan Incorporated (Career Skills) 1998Wyoming Incorporated (Social Studies) 2002Arkansas Incorporated (Economics) 2005Arizona Incorporated (Economics) 2005Louisiana Incorporated (Free Enterprise) 2005South Dakota 0.5 Credit (Economics or Personal Finance) 2006North Carolina Incorporated (Economics) 2007Georgia Incorporated (Economics) 2007Idaho Incorporated (Economics) 2007Texas Incorporated (Economics) 2007Utah 0.5 Credit 2008Colorado Incorporated (Economics, Math) 2009South Carolina Incorporated (Math, ELA, Social Studies) 2009Missouri 0.5 Credit 2010Iowa Incorporated (21st Century Skills) 2011Tennessee 0.5 Credit 2011New Jersey 2.5 Credits (Economics or Personal Finance) 2011Kansas Incorporated (Economics) 2012Oregon Incorporated (Social Studies) 2013Virginia 0.5 Credit 2014Florida Incorporated (Economics) 2014

PFL mandate data are from Stoddard and Urban (2020). States marked Incorporatedrequire personal finance coursework in the required course denoted in parenthesis. Stateswith listed credit requirement require the denoted number of credits in a standalonerequired personal finance course. States with a choice of Economics or Personal Financehave personal finance course standards in both courses.

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4 Empirical Strategy

4.1 Identification

To motivate the estimating equation introduced in the next section supposestate level graduation requirements divide students into those in states that requirehigh school students to complete PFL coursework and those not required. Usinga difference-in-differences framework, the effect of the required coursework on anoutcome is estimated using the equation

H8BC = + ����BC + �B + �C + �8BC , (1)

where �BC denotes whether state B had a binding mandate for cohort C and �B and�C are state and year fixed effects. H8BC denotes an outcome variable for individual8 belonging to graduating cohort C from state B.23 The outcome variable can berewritten using the potential outcomes framework so that

H8BC = H1,8BC · �BC + H0,8BC · (1 − �BC)where H1,8BC denotes the outcome for an individual if they are bound by a statemandate and H0,8BC denotes the outcome if the same individual is not bound by astate mandate. In reality, the researcher only observes either H1,8BC or H0,8BC for anygiven individual. However, if the researcher assumes students in states not boundby a state mandate evolve similarly to the unobserved non-mandated students inmandated states, ��� can be interpreted as the Average Treatment Effect on theTreated (ATT). More formally, suppose there are only two cohorts (C = 0, 1) andthe state adopting a mandate adopts for the second cohort (C = 1). The requisiteParallel Trends Assumption states that

�[H0,8B1 − H0,8B0 | �B1 = 0] = �[H0,8B1 − H0,8B0 | �B1 = 1].Under this assumption, observed outcomes for students in the non-adopting

states are used as the unobserved counter-factual outcomes for students in theadopting states and the parameter ��� captures the impact of the state adoptedpersonal finance education on the outcomes for the students who were treated.

However, consider the casewhere outcomes are only observed at the university-level for university 9. Suppose there exists a function� thatmaps each student 8 ∈ ℐto a university 9 ∈ J .24 The outcome .9� is defined as

.9� B1|�9� |

∑8∈�9�

H8BC

23In this example, the data are repeated cross section and an individual 8 is unique to a cohort Cand H8BC is only observed once per individual.

24For example, the universities can be indexed such that J = {0, 1, .., �} such that 9 = 0 denotes

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where �9� is the set of students that attend school 9, |�9� | is the number of studentsin the set �9�, and � = C + :8 for some :8 which defines the number of periodsbetween graduating high school and appearing in the university-level outcome forstudent 8. Under the enumerated assumptions below, I show in Appendix A.1 thatthe parameter ��� can be consistently estimated using the aggregated estimatingequation:

.9� = + ���pctBound9� + � 9 + �� + 4 9� (2)

where the term attached to ��� , pctBound9�, corresponds to the fraction of thecohort � for university 9 that were bound by state personal finance education man-dates. The necessary assumptions for identification are:

1. Parallel Trends Assumption: �[ΔH0,8BC | �B(8)C = 0] = �[ΔH0,8BC | �B(8)C = 1] ∀C2. Cohort Matching Assumption: :8 = : ∀83. Stability of University Mapping: �( 8 , �B(8)C = 1) = �( 8 , �B(8)C = 0)

As discussed above, we require the Parallel Trends Assumption in order to sat-isfy the micro-level difference-in-differences identification strategy. Next, it shouldbe the case that for all 8, :8 = :. If students in the same high school cohort C enter intodifferent university repayment cohorts � then it is possible that PFLmandates beginaffecting .9� prior to the first mandated cohort as matched by :. Lastly, it must bethe case that assignment of�BC does not change the choice of university for students.If students respond to personal finance education by altering the assignment to �9�,then the estimate from the aggregated specification captures ��� plus any potentialcompositional change in �9� that might affect .9�. Under these assumptions, we havethat Equation (2) consistently estimates ��� which is the causalATT (Average Treat-ment Effect on the Treated) estimated from themicro-level difference-in-differencesspecification.25

Stoddard and Urban (2020) present evidence in support of both the ParallelTrends Assumption and the Stability of University Mapping Assumption. First,they present evidence that states that adopt mandates are not observably differentnor are they trendingdifferently than states that didnot adopt amandate in theyearssurrounding adoption. Further, they present evidence that students from statesthat ultimately adopted a mandate did not have significantly different financialaid outcomes for cohorts prior to mandates adoption. These results suggest thatmandated states and non-mandated stateswere trending similarly prior tomandateoption which lends evidence toward the Parallel Trends Assumption. I also presentevidence in Section 5.2.2 that universities that received more mandated studentswere not trending differently in student loan repayment outcomes.

no university attendance and 9 = 1, ..., � denotes university attendance.25The full derivation is reported in Appendix A.1.

14

To help inform the Cohort Matching Assumption, Figure 2 shows the distribu-tion of the month students in the 2003 incoming college cohort entered repayment.The modal month students entered repayment is 51 months after entering college.This timing is consistent with a student entering college in August, graduatingin May of her fourth year, and entering repayment in November (after the sixmonth grace period). From this data, 43% of the repayment cohort enter repaymentbetween 48 months and 72 months after entering college. This suggests that a plu-rality of students will enter the College Scorecard data six years after high schoolgraduation. As such, I set : = 4 for student loan debt upon entering repaymentand : = 6 for student loan repayment outcomes to match this trend. While theseassumptions match the modal student loan borrower, the data show a significantshare of students entering repayment prior to 42 months since entering college. Ifthese are students bound by personal finance education mandates, it is possiblethey contribute to a repayment cohort that is inconsistent with the assumption of: = 6. To test sensitivity of this assumption to the main results, I present the resultsof a flexible event study specification in Section 5.2.2 which tests whether thereare intermediate effects of treated students potentially entering repayment prior to: = 6.

Figure 2: Month Entering Repayment for 2003 High School Cohort

0%

5%

10%

15%

20%

25%

0 12 24 36 48 60 72 84 96 108 120 132 144Month entering repayment (relative to college entry)

The figure above plots a histogram of the month a borrower enters repayment relative to the monththey enter college for four-year college students who did not attend graduate school. The sampleincludes federal student loan borrowers from the cohort entering college in the 2003-2004 academicyear. Students who attended graduate school are removed since they would mechanically enter intorepayment at a later month. Total student counts are collapsed into six month bins and nationallyrepresentative weights are used to create cohort shares.Source: U.S Department of Education, National Center for Education Statistics, 2004/2009 BeginningPostsecondary Students Longitudinal Study Restricted-Use Data File.

15

Lastly, identification relies on the third assumption, Stability of UniversityMap-ping. In essence, the estimate of �would be biased if students exposed to PFLman-dates changed their college enrollment decision. Using a difference-in-differencestrategy with micro-level data, Stoddard and Urban (2020) present evidence thatstudents bound by mandates were no more likely to choose to attend college norwere they anymore likely to attend college full- or part-time. Further, these studentswere no more likely to attend a private university, a university with lower tuition,an in-state university, or a four-year (versus two-year) university. In addition tothese findings, I present evidence in Appendix A.3.1 that states adopting mandatesdid not send their college seniors to different types of schools after themandate wasbinding. I also estimate an alternative specification in Appendix A.4.1 that does notrequire the Stability of University Mapping Assumption.

4.2 Dose Response Specification

To implement the proposed specification above, I begin by quantifying the shareof each incoming cohort bound by PFL mandates. Variation at the university-levelis driven primarily by state adoption of mandates but is also augmented by stateshares of incoming cohorts. When a state changes course standards for high schoolgraduation, all future high school students within the state are affected by thischange. When these students graduate high school and proceed to college, univer-sities that receive these students are now populated by these affected students. Thisis most often universities within the adopting state, however across-state migrationof high school students to colleges allows for spillovers from adopting states tonon-adopting states. In addition, students from non-adopting states drive downthe exposure at colleges in adopting states.

I use previous state of residence data from the Integrated Postsecondary Ed-ucation Data System (IPEDS) to track within and across-state migration of highschool students to colleges. For each university 8 and incoming cohort C, I constructpctBound8C by interacting the state-by-year mandate status of state 9 for cohort C(pfMandate9C) with the number of students attending university 8 in cohort C fromstate 9 (enroll8 9C). The total number of mandated students is then divided by thetotal incoming cohort count from all 50 states and D.C. for cohort C:

pctBound8C =

51∑9=1

pfMandate9C × enroll8 9C

51∑9=1

enroll8 9C. (3)

Figure 3 shows an example of how pctBound8C evolves over time for a selectgroup of Tennessee universities. The first graduating class bound by Tennessee’spersonal finance mandate was the class of 2011. Typically public universities re-ceive a large share of their student body from within the state. However, public

16

Figure 3: Examples of Within State Variation in pctBound from Tennessee

University of Tennessee Knoxville

Tennessee State UniversityVanderbilt University

Christian Brothers University

← TN adopts0.00

0.25

0.50

0.75

1.00

1995 2000 2005 2010 2015

% bound by PFL mandates

The figure above plots pctBound8C as constructed in Equation (3) for each university over time. Dataon previous state of residence come from IPEDS. State of residence data that are not submitted toIPEDS in odd years are interpolated linearly from neighboring even years. The state of Tennesseeadopted a personal finance mandate that was first binding for the class of 2011 as shown by theshaded region in each plot.

universities like University of Tennessee Knoxville and Tennessee State Universitystill differ in the share of students from within-state which drives variation in pct-Bound after the state adopts a PFL mandate. This heterogeneous impact is evenmore stark for private universities like Vanderbilt University and Christian BrothersUniversity. Despite the private status, the impact of Tennessee’s mandate adoptionis larger for Christian Brothers University than for Tennessee State University whileVanderbilt University experiences a smaller shock to pctBound after 2011.

In addition to the within-state variation, high school students attending collegein other states cause non-adopting states to be affected by mandates in adoptingstates. Figure 4 shows the state level equivalent of pctBound8C where the studentbodies of all universities within a state are aggregated. When Georgia adopted amandate binding for the class of 2007, Alabama universities experienced a corre-sponding increase in pctBound8C due to Georgia’s adoption. Additionally, Alabamauniversities experienced subsequent increases in pctBound when Tennessee andFlorida adopted in 2011 and 2014, respectively.

I exploit this unique source of exogenous variation in personal finance educationexposure to estimate the effect of changes in pctBound8C on university-level studentloan repayment outcomes. The main specification for the dose response model asmotivated by Equation (2) is:

H8B ,C+: = �pctBound8C + �X8BC + �8 + �C + E8BC , (4)

17

Figure 4: Example of Across State Spillovers in pctBound

Georgia universities

Alabama universities

GA adopts TN adopts FL adopts

0.00

0.25

0.50

0.75

1.00

1995 2000 2005 2010 2015

pctBound

The figure above plots the state level equivalent of pctBound8C where all universities within a stateare aggregated. Data on previous state of residence come from IPEDS. Georgia’s mandate was firstbinding for the class of 2007. Alabama did not a adopt mandate during the sample period butis affected by Georgia’s adoption through students from Georgia high schools attending Alabamauniversities and again by Tennessee and Florida’s adoption.

where H8B ,C+: is an outcome for university 8 located in state B for high school cohortC and : is the number of periods between cohort C entering college and outcome Hbeing observed.26 The coefficient of interest is � which estimates the causal effectof increasing pctBound from zero to one.

A vector of control variables are also included in X8BC to control for other statelevel changes that might also affect federal student loan repayment. First, I includecontrols for the number of credit hours required for high school graduation formath, science, English, and social studies along with the total number of credithours required. Since the introduction of PFL state standards might be introducedat the same time as changes to other course standards, these controls ensure � isnot capturing the effect of changes to other course requirements. Next, I includestate level counts of high school staffing for teachers, support staff, and guidancecounselors. Changes to state standards might also be accompanied by other statelegislation that could increase students’ access to college counseling or changestudent-to-teacher ratios. I also include controls for whether cohorts had access tostate merit aid scholarships since these may affect where students choose to attendcollege and how much students pay to attend college. Lastly, I include a vectorof unemployment rates between periods C to C + : to control for the local labormarket students face during college and into loan repayment. The data sources and

26: = 4 for student loan debt upon entering repayment and : = 6 for student loan repaymentoutcomes.

18

construction of these variables are detailed more thoroughly in Appendix A.2.In the baseline specification, I cluster standard errors at the state level to allow for

correlation in the error term, �8BC , between universities in the same state B (Bertrand,Duflo, and Mullainathan, 2004; Cameron and Miller, 2015). However, since treatedstudents are migrating across states to attend college, universities in different stateslikely also experience common unobserved shocks. If this is the case, errors mightbe correlated for universities across states and, consequently, clustering at the statelevel may produce standard errors that are too small (Barrios, Diamond, Imbens,and Kolesár, 2012).

To address this concern, I conduct a randomization inference exercise in thespirit of MacKinnon and Webb (2020). I estimate many “placebo” replications ofEquation (4)where pfMandate9C is drawn from {0, 1} at random. In each replication,I construct placebo pctBound8C using the randomly drawn pfMandate9C and applythe observed enroll8 9C . I then estimate Equation (4) using the placebo pctBound8Cto generate placebo �̂ estimates. Since the states adopting mandates in the placeboreplications are drawn randomly, it must be the case that the � estimates fromthis exercise equal zero on average. If �̂ estimated using the observed pctBoundmeasure is a sufficiently extreme value in the distribution of placebo estimates, thenull hypothesis of no treatment effect can be rejected.

The empirical p-values generated in this algorithm use the distribution of es-timated � coefficients without regard to the standard errors or any assumptionsabout the correlation structure of the data generating process. Instead, the underly-ing data generating process of students migrating to universities is captured in theempirical distribution of � estimates. As a result, the empirical p-values are robustto both within- and across-state correlation of universities driven by enroll8 9C . Thisalgorithm and a comparison of p-values using cluster robust standard errors andp-values using the randomization algorithm are detailed in Appendix A.3.

4.3 Event Study Specification

Identification of the causal effect of PFL education on student loan repaymentoutcomes relies on the Parallel Trends Assumption. This assumption is not directlytestable since counter-factual outcomes for treated units are unobserved. Instead, Ipresent evidence that universitiesmore exposed to PFLmandateswere not trendingdifferentially prior to the adoption of mandates by estimating a flexible event studyspecification. The event study specification includes a vector of binary variablesin which each variable represents a time period relative to the start of treatmentfor units experiencing an event. Each parameter then captures the difference inoutcomes between units experiencing an event and units not experiencing an eventduring the time period relative to treatment. In this context, the treatment variableis not discrete and thus care must be taken to define the first period of treatment. Idefine a university event as a year-over-year change in pctBound8C of 50 percentage

19

points or larger:

event8BC = 1 · {pctBound8C − pctBound8 ,C−1 ≥ 0.5}. (5)

I choose the 50 percentage point threshold to ensure a university can onlyexperience a single event. Table A.5 details the number of universities experiencingan event by this definition in each academic year along with the states adopting ineach year. Between 1996 and 2014, 524 universities experience an academic yearin which the adoption of at least one mandate changes pctBound8C by at least 50percentage points. Although there are a few early adopting states, most of theevents occur for the high school graduating cohorts of 2005 and later. As a result,there is more outcome data available for the periods prior to an event than for theperiods after an event. Hence, the test for pre-trends in student loan outcomes willbe more precisely estimated than the dynamic effect after adoption. The estimatingequation for the event study is identical to Equation (4) aside from the event studyparameters:

H8B� =

0∑9=−2

�9event8B ,C+9 +10∑9=2

�9event8B ,C+9 + �X8BC + �8 + �� + �8B�. (6)

In this specification, the event occurs in period C and a separate parameteris estimated for each period relative to an event with period C + 1 acting as thereference period.27 This results in ten estimated parameters across the event space.Since the College Scorecard only contains eight years of data for the repaymentrate, the window for each university’s outcome will not span the entirety of therange of event study parameters. Hence, the event study coefficients represent acombination of the dynamic effect of each university’s change in outcomes over timeplus a heterogeneous effect of universities entering and exiting the identificationof the parameter space. This is more clearly shown in Figure 5 which plots theidentifying variation of each event across the event study parameters. Since the datais both right and left censored, the universities that identify the pre-period (periodsC−2 through period C) are largely universities located in the states adopting after the2008 high school graduating class. On the other hand, the universities identifyingthe post-period (periods C + 6 through C + 8) are the states adopting in 2008 andprior. The parameters corresponding to periods C + 2 through C + 5 represent anintermediate range in which it is possible that treated students enter the Scorecarddata if they leave college prior to the assumed four year spell. This intermediaterange of parameters serves as a test of the Cohort Matching Assumption testing forchanges to repayment outcomes as a result of non-completing treated students.

27Since it takes at least one year for the repayment rate outcome to be observed, period C + 1 is thelast period before treated students can begin contributing to a university’s repayment rate for eachuniversity. A treated student entering the repayment rate data in year C + 1 would be a student whoseparated from college prior to the end of the first year.

20

Figure 5: Contribution to Event Study Parameters by University Event Year

pre-period intermediate post-period2002200320042005200620072008200920102011201220132014

Even

t Yea

r

t-2 t-1 t t+1 t+2 t+3 t+4 t+5 t+6 t+7 t+8

Periods relative to event

The above plot shows how each university contributes to each event study parameter by the yearof university event. Universities experiencing an event in 2009 and later do not contribute to thepost-event parameters while universities experiencing an event before 2007 do not contribute to thepre-event parameters. States adopting between 2006 and 2008 contribute to both the pre-period andpost-period parameters.

5 Results

5.1 Student Loan Debt

I test for changes in federal student loan borrowing by estimating Equation (4)for various measures of cohort student loan debt upon entering repayment. Table 3presents these results with moments of the cohort original balances in Panel Aand median student loan debt for subsamples of the student body in Panel B. Theestimates presented in Panel A suggest minimal changes to student loan borrowingacross thedistribution. No estimate is statistically different fromzero and eachpointestimate is proportionally small. The point estimates suggest small reductions inborrowing at lower student loan levels and small increases in borrowing at theupper ends of the distribution as a result of a university moving from no studentsto all students bound by a mandate. Overall, the results point to a shift away fromlower levels of borrowing towards higher levels of borrowing associated with PFLmandates, however none of these point estimates is statistically significant at eventhe 10% level.

Panel B shows the impact of personal finance mandates on the median studentloan debt for various subsamples of the student body. The results suggest minimaladjustments to borrowing for first generation, low income, and middle income stu-

21

Table 3: Dose Response Estimates: Student Loan Debt Upon Entering Repayment

A. Moments of the Cohort Student Loan Debt Distribution

(1) (2) (3) (4) (5)10th 25th 50th 75th 90th

pctBound -47.9 -239.1 -259.8 73.7 353.6(84.8) (176.4) (372.1) (346.8) (442.0)

Universities 1,370 1,383 1,386 1,383 1,370Outcome Mean 2552.7 4418.2 10225.7 18269.7 25380.8Percentage Effect -1.9% -5.4% -2.5% 0.4% 1.4%

B. Median Debt by Subsamples of the Cohort Student Body

(1) (2) (3) (4)First Gen Low

IncomeMiddleIncome

HighIncome

pctBound -100.1 194.7 -296.9 -763.4**(419.6) (377.6) (365.6) (374.7)

Universities 1,376 1,380 1,371 1,368Outcome Mean 9,819 10002.2 10202.8 10060.5Percentage Effect -1.0% 1.9% -2.9% -7.6%

Cohorts 1993-2012 1993-2012 1993-2012 1993-2012 1993-2012

Regressions are weighted using the number of students used to compute each outcome metric. Eachcolumn reports a coefficient from a separate regression where the independent variable is pctBoundand the outcome is denoted in the column header. The sample includes four-year universities. 10th,25th, 50th, 75th and 90th each represent the correspondent moment in a university’s student loandebt levels for students entering repayment. First Gen students are defined as students whose parentsdid not have a college degree. Low Income, Middle Income, and High Income students are definedas household income less than 30,000, between 30,000 and 75,000 and above 75,000, respectively.Controls include cohort weighted credit requirements in math, English, social studies, and scienceby high school graduation cohort and controls for state level high school staffing, and availability ofmerit aid scholarships. Also included are university and high school graduation year fixed effects.Standard errors clustered at the state level are presented in parenthesis. *** p<0.01, ** p<0.05, * p<0.1

dents with effect sizes of 3% and smaller and no statistically significant estimates.On the other hand, high income borrowers seem to be reducing student loan bor-rowing. The estimates suggest that a university moving to all mandated studentswould result in $763 smaller student loan balances for high income students, areduction of 7.6%.

These results suggest that personal finance course mandates do little to affecttotal student loan borrowing upon entering repayment. This is likely due to a fewkey facts from the literature. First, over 70% of student loan borrowers enteringcollege between 2001 and 2005 took out the maximum amount of student loans(Black et al., 2020). If demand for federal student loan dollars for these studentsis higher than the federal limit, borrowing even after adjustment due to the infor-mation intervention may remain at the federal maximum loan amount. Second,

22

experimental evidence suggests that many student loan borrowers do not makean active choice about how much to borrow (but only whether to borrow) even afterbeing providedwithmore information about borrowing options (Marx and Turner,2019a). As such, borrowers may continue to bunch at borrowing limits despite PFLcoursework. On the other hand, the finding that higher income students reduceborrowing may be due to the larger choice set of alternative borrowing optionsavailable through either family wealth or private student loans which often requirecredit-worthy co-signers.

5.2 Student Loan Repayment

5.2.1 Dose Response Specification

The results from the estimation of Equation (4) for the cohort default rate andthe repayment rate are presented in Table 4. Column 1 reports the estimates for thetwo-year cohort default rate while Columns 2 through 6 report the estimates for theoverall cohort and the various subsamples of the repayment cohort for the one-yearrepayment rate. The effect of personal finance mandates on defaults suggests areduction of 0.2 percentage points (a 5% reduction from the mean) associated witha full dose treatment of the incoming cohort. The magnitude of this estimate iseconomically meaningful but is not statistically different from zero at conventionallevels.28

Columns 3 and 4 suggest that increased exposure to personal finance educationmandates improves the one-year repayment rate for both first generation and lowincome students. The point estimates translate to a 2.4 and 2.3 percentage pointincrease in the repayment rate which corresponds to improvements of 4.5% and5.1% for first generation and low income students, respectively, with both resultssignificant at the 5% level.29 The point estimates for the overall repayment cohortand for middle and high income students are all positive, but are not statisticallydifferent fromzero. This pattern suggests that personal finance educationmandatesimprove the one-year repayment rate for first generation and low income students.

28The results are similar for the default rate if the sample years are limited to match the dataavailability years of the repayment rate analysis. The estimate is also not statistically significant usingthe randomization inference algorithm in Appendix A.3.

29Appendix A.3 compares the CRVE p-values to the p-values computed using the randomizationinfection algorithm described in Section 4. Both of these results are also statistically significant at the5% level using the RI-� algorithm.

23

Table 4: Dose Response Estimates: Cohort Default Rate and Repayment Rate

Default Rate Repayment Rate

(1) (2) (3) (4) (5) (6)Overall Overall First Gen Low

IncomeMiddleIncome

HighIncome

pctBound -0.002 0.013 0.024** 0.023** 0.009 0.010(0.447) (0.168) (0.029) (0.034) (0.344) (0.348)

Universities 1,386 1,384 1,340 1,354 1,319 1,317Cohorts 1993-2006 2001-2008 2001-2008 2001-2008 2001-2008 2001-2008

Outcome Mean 0.042 0.594 0.536 0.458 0.631 0.749Percentage Effect -5.0% 2.2% 4.5% 5.1% 1.5% 1.3%

Regressions are weighted using the number of students used to compute each outcome metric. Each columnreports a coefficient from a separate regression where the independent variable is pctBound and the outcomeis denoted in the column header. The sample includes four-year universities. Default rate analysis includeshigh school graduating classes 1993 through 2006 and repayment rate analysis includes high school graduatingclasses 2001 through 2008 due to data availability. First Gen students are defined as students whose parents didnot have a college degree. Low Income, Middle Income, and High Income students are defined as householdincome less than 30,000, between 30,000 and 75,000 and above 75,000, respectively. Controls include cohortweighted credit requirements in math, English, social studies, and science by high school graduation cohortand controls for state level high school staffing, and availability of merit aid scholarships. Also included areuniversity and high school graduation year fixed effects. P-values using standard errors clustered at the statelevel are presented in parenthesis. *** p<0.01, ** p<0.05, * p<0.1

5.2.2 Event Study Specification

I provide evidence in support of the Parallel Trends Assumption and the CohortMatchingAssumption in Figure 6which reports the coefficients and 95% confidenceintervals for the estimation of Equation (6) for the repayment rate subgroups. Inall four panels, there is no differential trend between universities experiencingan event and those not experiencing an event prior to treated students enteringcollege. Further, there does not appear to be a significant effect on universityrepayment rates during the intermediate periods for any of the subsamples. Theestimated coefficient for period C + 2 is negative for all groups and represents thesmallest parameter estimate, but is rather small inmagnitude. Although none of theintermediate estimates is distinguishable fromzero, theupward trend suggests non-completers exposed to personal finance mandates may also be better at repayingstudent loans. The estimates for the post-period parameters for low income (firstgeneration) students range from 1.8 percentage points (1.1 percentage points) inperiod C + 6 to 3.3 percentage points (3.6 percentage points) in period C + 8 which isconsistent with the point estimates presented in themain specification. The growthin the point estimates from period C + 6 to C + 8 suggests either improvements in

30If the quality of instruction improves over time, it should be the case that the effect of mandateson subsequent cohorts is larger than for the first cohort. On the other hand, if the treatment effect islarger for those who take longer than four years to graduate, we would expect the treatment effect togrow as the first treated students begin to enter repayment for : > 6.

24

the treatment effect over time or a “catching-up” effect of students who take longerthan four years to graduate college.30 The results in Panels C and D for middle andhigh income students suggests no significant effect until period C + 8 and is largelyconsistent with the muted estimates presented in Table 4.

Figure 6: Event Study Coefficients for Sample of Public Universities

pre-period intermediate post-period-0.05

0.00

0.05

0.10

t-2 t-1 t t+1 t+2 t+3 t+4 t+5 t+6 t+7 t+8

A. First Generation

pre-period intermediate post-period-0.05

0.00

0.05

0.10

t-2 t-1 t t+1 t+2 t+3 t+4 t+5 t+6 t+7 t+8

B. Low Income

pre-period intermediate post-period-0.05

0.00

0.05

0.10

t-2 t-1 t t+1 t+2 t+3 t+4 t+5 t+6 t+7 t+8

C. Middle Income

pre-period intermediate post-period-0.05

0.00

0.05

t-2 t-1 t t+1 t+2 t+3 t+4 t+5 t+6 t+7 t+8

D. High Income

Each panel in the above figure presented the vector of event study parameters with period C + 1omitted as the reference period. Since the repayment rate data takes at fewest one year to enterthe College Scorecard, it is not possible for a member of high school cohort C to contribute to therepayment outcome in C+1. However, early separators can contribute to the parameters C+2 throughC + 5. Period C + 6 represents students who spend four years in college and periods greater than C + 6represent students from cohort C who spent longer than four years in school or students in cohortsgreater than C which were also bound by PFL mandates.

In total, these results present evidence in support of the Parallel Trends As-sumption and in support of the Cohort Matching Assumption. In each event studyspecification, the coefficients corresponding to periods prior to an event are bothsmall and indistinguishable from zero. The same is true for each of the parameterscorresponding to periods in which treated non-completers might contribute to theuniversity repayment rate. Lastly, the parameters corresponding to the post-periodssuggest that first generation and low income students have higher repayment rates.The point estimates suggest that when the third cohort after the event has spentfour years in college, repayment rates for first generation and low income studentsare 3.6 and 3.3 percentage points higher, respectively.

25

5.3 Channels for Information Intervention

In this section, I investigate the primary information channel thatmight improverepayment outcomes by testing whether students who were bound by personal fi-nance education mandates in high school are better able to answer questions aboutfinancial literacy and federal student loans. I use micro-level data from a nationallyrepresentative survey of college students, the National Postsecondary Student AidSurvey (NPSAS). The 2016 wave of the NPSAS began asking college students threefinancial literacy questions and three questions pertaining to knowledge of federalstudent loan repayment.31 These new data provide insights into the financial liter-acy of current college students that was previously not available. However, sincethese questions are only included in one survey wave, comparisons of mandatedstudents to not mandated students from the same state largely rely on studentssurveyed at different ages.32 Regardless, the novelty of the questions asked in thissurvey necessitate its use. The estimating equation takes the form

H8BC = �pfMandateBC + �-8BC + �B + �C + �8BC , (7)

where H8BC is a binary variable for whether respondent 8 from state B observedgraduating from high school in year C correctly answered a particular question.-8BC includes a vector of binary control variables which includes race, gender, andyear in college and the vector of state-by-graduation year controls for merit aid,high school staffing, and credit requirements as in Equation (4). � is the parameterof interest which captures the difference in the probability of correctly answeringa particular question between mandated and non-mandated students. Lastly, Iinclude state and high school graduation year fixed effects and I use the includedsurvey weights so the analysis is nationally representative. Standard errors areclustered at the high school state level.

Figure 7 plots the coefficient estimates and 95% confidence intervals from theestimation of Equation (7). The point estimate for each of the three financial literacyquestions is less than a half a percentage point and the null hypothesis cannotbe rejected for any estimate. Further, there is no significant change in the totalnumber of correct answers as a result of a binding personal finance mandate.33On the other hand, each of the estimates for the three loan literacy questions ispositive ranging from 1.3 to 3.3 percentage point increases in the probability ofa correct answer. The largest effect is for the question asking borrowers whetherthe federal government can garnish wages for non-payment of federal studentloans. Additionally, respondents answered 3% more questions correctly if they

31The questions are detailed in Table A.7.32Additionally, the 2016 wave of the NPSAS largely contains students that graduated high school

after the period between 2001 and 2008 which were the cohorts showing improvement in repaymentrates.

33The full table of coefficients and standard errors along with the effect on the number of correctanswers can be found in Table A.6.

26

Figure 7: Difference-in-Difference Estimates for Financial Literacy and Loan Liter-acy from NPSAS:16

Q1:Interest

Q2:Inflation

Q3:Stocks

Q1:Credit

Q2:Garnish Wages

Q3:Withold Tax-0.050 -0.025 0.000 0.025 0.050

Financial Literacy Questions (NPSAS)Loan Literacy Questions (NPSAS)

The abovefigures plot the point estimates and 95%confidence intervals for the difference-in-differencecoefficients using the NPSAS.Question text is available in Table A.7 and a full table of coefficient esti-mates and standard errors is available in Table A.6.Source: U.S Department of Education, National Center for Education Statistics, Restricted-use Na-tional Postsecondary Student Aid Study 2016.

were bound by a personal finance mandate.The evidence suggests that mandated students are more knowledgeable about

regulations governing federal student loans. If this is the case, student loan borrow-ers may be better able to repay loans due to this increased familiarity with the rulesand regulations for their loans. These students might be more aware of income-driven repayment plans which have been shown to improve repayment progressand reduce delinquencies (Herbst, 2020) or of various forbearance or defermentoptions. On the other hand, since mandated students are more likely to know thefederal government can garnishwages for non-payment, theymay bemore inclinedto prioritize student loan debt over other types of consumer debt.

6 Discussion

The findings in this paper extend the literature on personal finance educationmandates and federal financial aid in several key dimensions. I find that studentswho were bound by PFL mandates in high school were better at repaying studentloan balances. The impact is largest and most precisely estimated for low incomeand first generation students which is consistent with findings in the literature

27

showing course mandates have large effects for more vulnerable populations (Stod-dard and Urban, 2020; Goodman, 2019). The results suggest that low income andfirst generation students are roughly 5% more likely to have paid down some oftheir original balance one year after entering repayment. Despite some suggestiveevidence of improvements, I cannot conclude that mandates have any meaningfulimpact on the cohort default rate. However, this result is likely not surprising sincestudent loan default is a more rare and adverse outcome while repayment progressis a more sensitive measure.

I also find that median student loan balances are not significantly declining asa result of personal finance education mandates for first generation or low incomestudents who are better at repaying loans. This result is likely due to findingsin the literature that suggest a majority of student loan borrowers borrow at thefederal maximum (Black et al., 2020). If so, students may indeed intend to readjustborrowing, but maximum federal student loan limit remains binding at the newoptimum. On the other hand, I find that high income students reduce borrowingby around 8% which may explain the muted improvement in repayment rates forhigh income students.

These findings suggest that, despite little change to the amount of studentloan debt when a borrower enters repayment, first generation and low incomestudents have smaller student loan balances one year after entering repayment ifthey were bound by a personal finance education mandate during high school.But are short term improvements in student loan repayment indicative of longerterm improvements? Table 5 reports a summary of various long term repaymentoutcomes for a nationally representative sample of college students entering collegein 2003. The sample is split by whether a student had paid down at least one dollarof original balance one year after entering repayment. Students in this cohortwho were able to pay down at least a dollar of their student loan debt one yearafter entering repayment were significantly better at repaying their loans 12 yearsafter entering repayment. These students paid down nearly half of their loanswhile those not achieving the benchmark still owed 81% of their original balance.They were also half as likely to have defaulted on a student loan and were 19percentage points more likely to have ever repaid their student loans. Althoughnot causal estimates, these comparisons suggest that improvements in the one-yearrepayment rate caused by PFL mandates could also lead to large future studentloan repayment success for mandated students. Since federal student loan balancesare forgiven after 20 or 25 years of payments, these improvements in repayment arelikely to reduce the total amount of forgiven federal student loans.

Lastly, I also explore by which primary information channel these improve-ments function. Borrowers may be better able to repay student loans because theyare more financially literate, they better understand the rules governing federalstudent loans, or some combination of both. I find no evidence that students boundby personal finance education mandates are better able to answer typical finan-

28

Table 5: Long-term Repayment Outcomes Conditional on One Year Repayment(Beginning Postsecondary Students 2004)

Paid down principal after oneyear

Outcome 12 years after entering col-lege

Yes No

Percent owed on balance 0.51 0.82Ever defaulted on loan 0.12 0.24Ever paid off loan 0.58 0.37Remaining balance $22,086 $36,814

Total Weighted Population 537,990 425,930

Source: U.SDepartment of Education, National Center for Education Statistics, 2004/2009Beginning Postsecondary Students Longitudinal Study Restricted-Use Data File with the2015 FSA Supplement. Estimates come from author’s calculations. One year repaymentrate metric is constructed by calculating the outstanding student loan balance one yearafter entering repayment and comparing to the outstanding balance upon entering re-payment. Only borrowers who had entered repayment by the end of 2009 are consideredto maintain consistent end dates.

cial literacy questions. This finding does not necessarily imply that PFL mandatesare ineffective at improving financial literacy or financial outcomes. It is possiblethat improvements in financial literacy depreciate quickly after high school and/ornon-mandated peers quickly catch up. It is also possible that the ability to answerfinancial literacy questions is a poor proxy for financial skills that tangibly improvefinancial outcomes. Several findings in the literature show improvements in finan-cial outcomes, aside from student loan repayment, associated with PFL mandates(Urban et al., 2018; Stoddard and Urban, 2020; Brown et al., 2016; Harvey, 2019).

On the other hand, I present evidence that students bound by personal financemandates are more knowledgeable about the federal financial aid system. Studentsbound by mandates are more likely to correctly answer questions about federalstudent loans. This suggests that students bound by the mandates may be betterable to repay student loans in part due to increased familiarity with the federalstudent loan system. If this is the case, personal finance mandates might not benecessary to improve student loan outcomes if the federal loan system were sim-plified. The results from this paper lend further evidence to the string of literaturethat shows potential benefits to a more streamlined federal financial aid systemwith fewer complexities that borrowersmust learn beforemaking postsecondary fi-

29

nancing decisions (Dynarski and Scott-Clayton, 2006; Bettinger, Long, Oreopoulos,and Sanbonmatsu, 2012; Novak and McKinney, 2011; Dynarski and Scott-Clayton,2013; Castleman, Schwartz, and Baum, 2015; Kofoed, 2017). However, the benefitsto personal finance educationmandates highlighted in this paper and in the relatedliterature indeed suggest that mandating personal finance education in high schoolcan improve financial outcomes for those students exposed to course material (Ur-ban et al., 2018; Stoddard and Urban, 2020; Brown et al., 2016; Harvey, 2019). Thesemandates may be evenmore effective if coursework no longer needed to be devotedto teaching students how to navigate the federal financial aid system but insteadfocused on more typical financial literacy topics.

30

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33

A Appendix

A.1 Derivation of Motivating Specification

In this section, I show that when the three assumptions are satisfied, the ag-gregated estimating equation, Equation (2), consistently estimates the difference-in-differences parameter, ��� . First, assume the following assumptions hold:

1. Parallel Trends Assumption: �[ΔH0,8BC | �B(8)C = 0] = �[ΔH0,8BC | �B(8)C = 1] ∀C2. Cohort Matching Assumption: :8 = : ∀83. Stability of University Mapping: �( 8 , �B(8)C = 1) = �( 8 , �B(8)C = 0)

where B(8) is the state of high school for student 8. First, define the function� : ℐ × D → J where ℐ = {1, ..., �}, D = {0, 1}, and J = {0, 1, ..., �}. ByAssumption 3, �(8 , �B(8)C = 1) = �(8 , �B(8)C = 0) so we can simplify this functionto �′ which maps ℐ → J such that �′(8) = 9 is independent of �B(8)C . Recall thedifference-in-differences specification using micro-level data is:

H8BC = + ����B(8)C + �B(8)C + �8BC , (8)

Using the assumption that :8 = : for all 8, we can define � B C + :. Define �9� equalto {8 : �′(8) = 9 , C = � − :} and define |�9� | as the number of students in �9�. Theaggregated outcome, .9�, is defined by

.9� B1|�9� |

∑8∈�9�

H8BC

which constructs the average of H for all students in the set �9�. Similarly, the sametransformation can be applied to the RHS of Equation (8):

.9� =1|�9� |

∑8∈�9�

[ + ����B(8)C + �B(8)C + �8BC

]=

1|�9� |

∑8∈�9�

+ 1|�9� |

∑8∈�9�

[����B(8)C

]+ 1|�9� |

∑8∈�9�

�B(8)C +1|�9� |

∑8∈�9�

�8BC

= + ���

∑8∈�9�

�B(8)C

|�9� |

+1|�9� |

∑8∈�9�

�B(8)C +1|�9� |

∑8∈�9�

�8BC

The first term in the specification trivially reduces to . The second termreduces to the share of students in �9� for which �B(8)C = 1 which we will defineas pctBound9�. Additionally, since the error term is assumed mean-zero in the

34

micro-level case conditional on observables and the Parallel Trends Assumption,the aggregated university-level error draws will also be conditionally mean-zerosince the allocation of students to universities is unchanged by �B(8)C . As a result,the university error term can be rewritten as an arbitrary mean-zero error term 4 9�.

.9� = + ���pctBound9� +1|�9� |

∑8∈�9�

�B(8)C + 4 9�

By the Parallel Trends Assumption, we can rewrite �B(8)C = �B(8) + �C . Further,

�B(8) can be rewritten as(∑B=1

�B · 1{B(8) = B} and the specification becomes

.9� = + ���pctBound9� +∑8∈�9�

(∑B=1

�B1 ·

{B(8) = B, 8 ∈ �9�

}|�9� |

+ 1|�9� |

∑8∈�9�

�C + 4 9�

.9� = + ���pctBound9� + �C +(∑B=1

�B

∑8∈�9�

1 ·{B(8) = B, 8 ∈ �9�

}|�9� |

+ 4 9�Since � = C + : by assumption, the time fixed effect is unchanged and �� is just

a change in notation. However, the last remaining term is more nuanced. Notethat this term is a reweighting of the feeder-state fixed effect in accordance withthe share of the cohort from each feeder state. For ease of interpretation, define thefollowing terms

StateShareB 9� B∑8∈�9�

1 ·{B(8) = B, 8 ∈ �9�

}|�9� |

, � 9 B)+:∑�=:

(∑B=1

�BStateShareB 9�

Adding and subtracting � 9 yields:

.9� = + ���pctBound9� + �C + � 9 −)+:∑�=:

(∑B=1

�BStateShareB 9� +(∑B=1

�BStateShareB 9� + 4 9�

= + ���pctBound9� + �C + � 9 +[(∑B=1

�B

(StateShareB 9� −

)+:∑�=:

StateShareB 9�

)]+ 4 9�

The remaining term in brackets represents the sum of transitory deviationsfrom the university’s mean share of students from each state multiplied by thefixed effect for each state. By the Stability of University Mapping assumption, thisterm is independent of the components of pctBound9�. Collecting this transitoryenrollment deviations term with 4 9�, we can rewrite the estimating equation as:

35

.9� = + ���pctBound9� + � 9 + �C + E 9�. (9)

Hence, under the three aforementioned assumptions, the aggregate university-level specification consistently estimates the micro-level difference-in-differencesspecification. Additionally, in Appendix A.4.1, I estimate an alternative university-level specification that holds StateShareB 9� fixed at initial levels. In this specification,the identification of ��� in the university-level specification is consistent even in thecase where students alter their college choice as a result of �B(8)C .

A.2 Data Appendix

A.2.1 College Scorecard

All data used in the analysis was pulled from the College Scorecard websiteusing the October 30, 2018 update. The subsequent updates (as of July 20, 2020)did not affect the measures from the NSLDS used in this paper.

The two main outcomes from the College Scorecard are the two-year cohortdefault rate and the one-year repayment rate. After leaving college, federal studentloan borrowers are granted a sixmonth grace period before theymust beginmakingmonthly payments. One year after entering repayment, borrowers fit into one offour mutually exclusive bins as depicted in Figure A.1.34 If the student is makingpayments on her loans and the balance is declining, this student fits in bin A. Ifthe student is making payments toward her loan but the payment is not sufficientto cover accruing interest (i.e. negative amortization), the student fits in bin B.35 Ifthe student has been granted forbearance or deferment of payments (and thus nopayments are required) and the balance is not declining, the student fits in bin C.If the student has not made any payments for 270 days, the student enters defaultand fits in bin D.36

The two-year cohort default rate is calculated in the College Scorecard by di-viding the total number of students in default (bin D) at the end of the two yearwindow by the total number of students in the repayment cohort (the sum of binsA, B, C, and D). The one-year repayment rate is calculated by dividing the numberof students who have paid down at least one dollar of their original principal (binA) one year after entering repayment by the total repayment cohort excluding those

34The College Scorecard database also includes the repayment rate for 3, 5, and 7 years, howeverthe data begins for all variables for FY 2006 and thus these variables have very small windows of dataavailability.

35Due to income-driven repayment plans, it is possible that the monthly minimum payment is notenough to cover the interest accruing each month. In this case, it is very unlikely the borrower willhave a declining balance without paying more than the monthly minimum payment.

36Default for students loans is atypical compared to other consumer debt. Upon default, there isno repossession of assets since the loans are unsecured. Rather, the federal government levies finesand allows loan services to garnish wages and tax refunds to collect outstanding debts.

36

Figure A.1: Repayment Status Bins for Repayment Cohort

A B C D

Making payments &paying down balance

Making payments & notpaying down balance

In forbearance ordeferment

In default

Repayment Rate = AA+B+C Default Rate = D

A+B+C+D

in default (the sum of bins A, B, and C). Those students in bin B (making paymentsbut facing negative amortization) and in bin C (not required to make payments andfacing negative amortization) both count against the repayment rate but are not indefault.

The repayment rate is first reported in the College Scorecard beginning withthe 2007-2008 academic year which includes students entering repayment in the2006 fiscal year.37 The most recent data in the Scorecard covers students thatentered repayment in the 2013 fiscal year.38 Beginning in FY2009, the Departmentof Educationbegangradinguniversities on the three-year cohort default rate insteadof the previous two-year cohort default rate. This change was a concerted effortto hold universities accountable for borrowers beyond two years after enteringrepayment. The College Scorecard continued to include the two-year cohort defaultrate through FY2011 but deferred to only posting the three year cohort default ratein subsequent years. Due to the change in the cohort default metric, I use thetwo-year cohort default rate in the available years between FY1995 and FY2011.

A.2.2 Integrated Postsecondary Education Data System

I collect previous state of residence data from the Integrated PostsecondaryEducation Data System (IPEDS). This data comes from the Compare Institutionstool on the IPEDS website. The data include years 1986 through 2016 for alluniversities in the Scorecard sample. From the Fall Enrollment category, I usethe “State of residence when student was first admitted” and counts of “First-time degree/certificate-seeking undergraduate students who graduated from highschool in the past 12 months.” These data were required to be submitted in: 2016,2014, 2012, 2010, 2008, 2006, 2004, 2002, 2000, 1998, 1996, 1994, 1992, 1988, and 1986.Universities could voluntarily provide this data in: 2015, 2013, 2011, 2009, 2007,2005, 2003, and 2001. I impute missing values by linearly interpolating between the

37The College Scorecard reports the one-year repayment rate as a two year rolling average inorder to reduce variability. Although this is not ideal for identification, I match the repayment rateoutcome using the first year a repayment cohort is reported in the data to match incoming collegecohorts to repayment cohorts. Any bias from this rolling average will work against detecting an effectof mandates on repayment since it will include one untreated cohort and the first treated cohort.

38For repayment cohort counts smaller than 30 students, the data is suppressed and thus thesesmall cells are omitted from the analysis.

37

nearest non-missing years. In addition, Appendix A.4.3 estimates Equation (4) byusing instrumented values of enrollment counts rather than linear interpolation.

A.2.3 High School Staffing Variables

I collect counts of state level high school staffing to use as controls in all specifi-cations. These data come from the Common Core of Data (CCD) and are accessedusing the educationdata Stata package from the Urban Institute. I pull these datafor the years 1993 through 2015 at the school district level. Counts for each ofthe following are collected and aggregated to the state level: total staff, full-timeequivalent total teachers, full-time equivalent total school support staff, total schoolguidance counselors, and total student support staff.

A.2.4 High School Graduation Requirements

I create a panel dataset of credit requirements for high school graduation at thestate-by-graduation-year level. These data are primarily sourced from the NationalCenter for Education Statistics (NCES) Digest of Education Statistics Chapter 2.These tables present snapshots in time of state credit requirements for each statealong with the first effective graduating cohort bound by the requirements. Thefirst table is from 1995 and I use these snapshots to track changes in graduationrequirements in: Total Credits, English/Language Arts, Social Studies, Math,and Science. The creation of this data required some decisions in which I try tofollow objective rules. First, not all states have state requirements for high schoolgraduation. States like Colorado deferred requirements to the district level. Forthese states, I impute the state requirements by substituting the national averagefor each graduating cohort for states with requirements and I include a binaryvariable denoting local control. Second, many states have multiple tracts studentscan select with different credit requirements for each track. When possible, I selectthe vector of graduating requirements that had the minimum standards. These aretypically obviouswhen the choice is between a “standard”diplomaandan “honors”diploma, however the definition can be more subjective when states allow studentsa technical career path. In these cases, I choose the standard diploma requirementsas the technical career path students are less likely to attend a four-year college afterhigh school graduation.

I supplement and cross reference the NCES data with data from the EducationCommission of the States 50-State Comparison: High School Graduation Require-ments (Macdonald, Dounay-Zinth, and Pompelia, 2019). When conflicts betweenthe sources arose, I tracked the course standards using state Department of Educa-tion websites to resolve discrepancies. This data is available upon request.

38

A.2.5 State Merit Aid

I use the definition of state merit aid availability at the state-graduation-yearlevel as defined by Sjoquist and Winters (2015). They define merit aid scholarshipsas “strong” and “weak”merit aid programs and I follow their convention. I includea binary indicator variable at the high school graduating cohort by year level forthe presence of weak and strong merit aid in each specification.

A.2.6 Constructing University Cohort Controls from State-by-Graduation-YearData

A vector of incoming cohort level controls are included in X8C . In a similarmanner to Equation (3), I create a vector of control variables for each incominguniversity cohort that is weighted by the state composition of the incoming cohort.I use high school graduation state 9 by high school graduation year C variables, G 9C ,combined with previous state of residence data, enroll8 9C , for university 8 from state9 in year C to construct an incoming university cohort measure for each variable in-8C :

X8C =

51∑9=1

x9C × enroll8 9C

51∑9=1

enroll8 9C, (10)

This vector includes the state level measures of high school staffing and highschool graduation requirements.39 In addition to these state weighted controls, X8C

also includes binary variables for whether the state of university offered a merit aidscholarship along with unemployment rates for periods C through C + :.

A.3 Randomization Inference Algorithm

The randomization inference algorithm used to compute the empirical p-valuesis based off the RI-� algorithm in MacKinnon and Webb (2020). I conduct 3000replications of Equation (4) for each outcome variable where the identifying varia-tion in the replication is randomly generated by supposing that the adopting statesdo not adopt and the non-adopting states do adopt.40 In each of these replications,it should be the case that the estimated treatment effect for the placebo replicationsis zero on average. Further, the estimated treatment effect using the observed pct-

39Not all states have high school graduation standards set at the state level. For states with no statestandards, the mean value across all states is used and a binary variable is included denoting localcontrol of high school graduation standards.

40I have also repeated this algorithm without taking into account observed adopting states andinstead drawing states and implementation years unconditionally. The results are similar for bothwhich further suggests the states and years of adoption are “as good as random.”

39

Boundmeasure should be a sufficiently extreme value in the distribution of placeboreplications. The algorithm proceeds as follows for each replication:

1. Split the sample of 50 states plus D.C. into two groups

Group A: States adopting a mandate binding for the class of 2008 andprior (13 states)Group B: States adopting a mandate binding for the class of 2009 andlater and states that never adopt a mandate.

2. Choose 13 states at random from Group B to slot into the mandate adoptionslots observed in the true data41

3. Use this selectionof states andadoptionyears togenerateplacebopfMandate9C .

4. Compute pctBound8C =

51∑9=1

pfMandate9C×enroll8 9C

51∑9=1

enroll8 9Cusing placebo pfMandate9C .

5. Estimate Equation (4) using the placebo pctBound8C .

6. Store �̂= .

Once all �̂= for = = 1, ..., 3000 are collected, the empirical p-value is computedusing:

?̄ =1

3000

3000∑==1

1 ·{|�̂= | ≥ |�̂CAD4 |

}(11)

Table A.1 replicates Table 4 and includes the p-values calculated from thisalgorithm. Across each outcome, the p-values using CRVE are always smallerthan the p-values using the RI-� algorithm, suggesting that there is indeed somecorrelation in error terms across states. However, these larger p-values do notchange the level of significance for the main results, namely the improvement inthe one-year repayment rate for low income and first generation borrowers.

A.3.1 SupportingEvidence for theStability ofUniversityMappingAssumption

This section presents further evidence (beyond the findings in Stoddard andUrban (2020)) in support of the Stability of University Mapping Assumption. Totest this assumption, I use the IPEDS previous state of residence data to track theflow of high school students from each state into the colleges they ultimately en-

41One adopting state in 1993, 1996, 1998, 2002, 2006 and 2008. Three adopting states in 2005. Fouradopting states in 2007.

40

Table A.1: Dose Response Estimates: Cohort Default Rate and Repayment Rate

Default Rate Repayment Rate

(1) (2) (3) (4) (5) (6)Overall Overall First Gen Low

IncomeMiddleIncome

HighIncome

pctBound -0.002 0.013 0.024 0.023 0.009 0.010(0.447) (0.168) (0.029)** (0.034)** (0.344) (0.348)[0.500] [0.219] [0.032]** [0.037]** [0.364] [0.456]

Universities 1,386 1,384 1,340 1,354 1,319 1,317Cohorts 1993-2006 2001-2008 2001-2008 2001-2008 2001-2008 2001-2008

Outcome Mean 0.042 0.594 0.536 0.458 0.631 0.749Percentage Effect -5.0% 2.2% 4.5% 5.1% 1.5% 1.3%

Regressions are weighted using the number of students used to compute each outcomemetric. Each column reportsa coefficient from a separate regression where the independent variable is pctBound and the outcome is denoted inthe columnheader. The sample includes four-year universities. Default rate analysis includes high school graduatingclasses 1993 through 2006 and repayment rate analysis includes high school graduating classes 2001 through 2008due to data availability. First Gen students are defined as students whose parents did not have a college degree.Low Income, Middle Income, and High Income students are defined as household income less than 30,000, between30,000 and 75,000 and above 75,000, respectively. Controls include cohort weighted credit requirements in math,English, social studies, and science by high school graduation cohort and controls for state level high school staffing,and availability of merit aid scholarships. Also included are university and high school graduation year fixed effects.P-values using standard errors clustered at the state level are presented in parenthesis. Empirical p-values usingrandomization inference are presented in brackets. *** p<0.01, ** p<0.05, * p<0.1

roll.42 Recall the IPEDS data includes the variable enroll8 9C which is the number ofstudents in the incoming cohort for university 8 who previously resided in state 9for incoming cohort C. Instead of aggregating student counts at the university-level,I can instead aggregate student counts at the previous state of residence level ac-cording to universities characteristics. This procedure generates the percent of highschool students from each state attending universities of a given type. Equation (12)illustrates an example of this variable construction using the university character-istic Public4yr8 , which equals one if a university is a four-year public college andSeniors9C is the total number of enrolled high school seniors for the graduatingcohort C.43

pctPublic4yr9C =

∑8∈�

Public4yr8 × enroll8 9C

Seniors9C(12)

The constructed variable, pctPublic4yr9C measures the percent of high schoolseniors from state 9 in cohort C who enrolled in a public four-year university. Icreate analogous variables for any two-year and four-year college and for two-year

42Stoddard and Urban (2020) perform a similar test using the IPEDS enrollment data and countsof the number of 18 year olds in a state in a given year.

43The variable Seniors9C comes from enrollment counts from the Department of Education’s Com-mon Core of Data.

41

and four-year public, private non-profit, private for-profit, and in-state universities.I use these constructedvariables as outcomemeasures for a state-by-yeardifference-

in-differences design to test whether the state adoption of a personal finance edu-cation mandate alters the share of students attending various types of colleges. Theestimating equation is similar to Equation (4):

H 9C = �pfMandate9C + �X9C + � 9 + �C + �9C , (13)

where H 9C is a state-level variable, such as pctPublic4yr9C , andpfMandate9C is a binaryvariable denoting whether state 9 had a binding personal finance mandate in effectfor cohort C. The vector -9C is the same set of state-by-graduation year level controlsas in Equation (4) and � 9 and �C are state and year fixed effects, respectively.44

Figure A.2: Difference-in-Differences Estimates for Changes to College Enrollment

Dependent variable mean: Dependent variable mean: Dependent variable mean: Dependent variable mean: Dependent variable mean:

0.161 0.439 0.152 0.296 0.002 0.137 0.007 0.006 0.146 0.292

-0.020

-0.010

0.000

0.010

0.020Any College Public Non-profit For-profit In-state

2-year Universities 4-year Universities

The figure above plots a separate difference-in-differences coefficient estimate and corresponding95% confidence interval where the independent variable is pfMandate and the outcome variable isdenoted for each column. Each outcome is reported for two-year universities with a square and four-year universities with a triangle. Control variables include state level counts of high school staffing,other high school graduation credit requirements for math, English, social studies, and science, andthe availability of state merit aid scholarships.

Figure A.2 presents point estimates and 95% confidence intervals for this speci-fication. All reported point estimates a smaller than a one percentage point change

44These controls include state level counts of school staffing, other course requirements for grad-uation, and the availability of state merit aid scholarships.

42

in either direction and no estimate is statistically different from zero at any con-ventional significance threshold. The results are consistent with the findings in theliterature which find no changes in college attendance or the choice of college asa result of a binding personal finance education mandate (Stoddard and Urban,2020).

Lastly, I test whether personal finance education mandates have any impact onthe probability a student earns a degree. If personal finance education leads tobetter matching of students to colleges or degree programs, students may be moresuccessful in college. As a result of graduation, studentswill likely have better labormarket outcomes whichwould lead to better repayment rates and a lower chance ofdefault. I use the American Community Survey (ACS) one-year samples from 2005-2017 to test whether students bound by personal financemandatesweremore likelyto hold a college degree or have ever attended college. The estimating equation forthese tests is identical to Equation (7). However, I remove students younger than22 as these students are unlikely to have earned a bachelor’s degree yet. Since theACS also does not ask respondents for the year of high school graduation, I assumerespondents graduate from high school in the year of their 18th birthday. I reportresults where either the state of birth or the state of residence is used in place ofstate of high school since this is also unobserved.

Table A.2 reports the results of this estimation on the (linear) probability ofearning a bachelor’s degree, the probability of earning an associates degree, and theprobability a respondent ever attended college. Odd numbered columns identifymandate status by birth state while even numbered columns use state of residence.The estimates across all columns suggest there is no effect of personal financeeducationmandates on the probability of earning a Bachelor’s degree, an associatesdegree, or having ever attended college. In total, I find little compelling evidenceto suggest that personal finance education mandates shift a high school student’sdecision to attend college nor the type of college they choose to attend.

43

Table A.2: Difference-in-Differences Estimates for Degree Completion from ACS

(1) (2) (3) (4) (5) (6)Bachelor’sEarned

Bachelor’sEarned

AssocEarned

AssocEarned

EverCollege

EverCollege

PF Mandate -0.000 0.000 0.001 -0.002 -0.006 -0.006(0.002) (0.002) (0.001) (0.002) (0.004) (0.005)

Observations 2,670,765 2,670,765 2,670,765 2,670,765 2,670,765 2,670,765Cohorts 2001-2008 2001-2008 2001-2008 2001-2008 2001-2008 2001-2008High School State Birthplace Residence Birthplace Residence Birthplace Residence

Outcome Mean 0.196 0.196 0.083 0.083 0.688 0.688Percentage Effect -0.2% 0.1% 0.7% -1.9% -0.9% -0.9%

Notes: Sample includes respondents from the 2005-2017 American Community Survey with a highschool diploma or higher that were born in the U.S. and 22 years of age or older. Controls includebinary variables for gender and race alongwith credit requirements inmath, English, social studies,and science by high school graduation year and state of residence, controls for state level high schoolstaffing, and availability of merit aid scholarships at the state level. Also included are state and highschool graduation year fixed effects. Standard errors are clustered at the state level. *** p<0.01, **p<0.05, * p<0.1

A.4 Alternative Specifications

In this section, I explore whether the results presented above are sensitive to thechoice of specification and the use of the continuous treatment measure.

A.4.1 Robustness to Changes in College Enrollment

In this section, I present evidence that the results presented above are robusteven if the Stability of University Mapping Assumption is violated. Note that inAppendix A.1, it was necessary to assume that the term[

(∑B=1

�B

(StateShareB 9� −

)+:∑�=:

StateShareB 9�

)]was independent of pctBound. For this specification, instead of assuming pctBoundis independent of the StateShare terms, I construct an alternate pctBound that holdsthe StateShare terms constant over the sample years. As such, Appendix A.4.1 nowequals zero since there canbenodeviation fromcurrent year state shares to themeanstate share of students over the panel. This specification is motivated by a “shift-share” framework inwhich exposure levels are held constant at initial levels and thevariation in the identifying variable is driven by an interaction of the constant sharesand an aggregate trend (Bartik, 1987). Hence, the identifying variation in thismodeldoes not rely on transitory changes in high school students’ college choice but rathereach university’s exposure to each state’s potential adoption of PFLmandates in the

44

period before PFLmandate adoption. Applying this framework to the constructionof pctBound, I construct enroll8 9 ,(which is themean enrollment of the students fromstate 9 at university 8 for a set of academic years (. The construction of �pctBound8Ctakes the form:

�pctBound8C = 51∑9=1

[enroll8 9 ,(enroll8 ,(

]× pfMandate9C . (14)

For this analysis, the set ( contains the IPEDS state of residence counts from1986through 1994 as this period largely contains state composition before the rollout ofpersonal finance mandates. Summing over all states and D.C. yields the mean totalenrollment enroll8 ,( for university 8 during the set of years (. Hence, the fixed shareof students from university 8 from state 9 can be derived as the ratio of enroll8 9 ,( toenroll8 ,(. When there is no change in PFL mandate adoption from year C to yearC + 1, there is no change in �pctBound8C to �pctBound8 ,C+1. However, if state � adoptsa mandate between graduating cohort C and graduating cohort C + 1, the differencein �pctBound8 ,C+1 and �pctBound8C is exactly equal to the ratio enroll8� ,(/enroll8 ,(, orstate �’s historical composition for university 8.

Figure A.3 plots the estimates from this alternative specification relative to theestimates from the baseline specification. For all outcome variables, the point esti-mates are largely unchanged between the baseline specification and the shift-sharespecification. In fact, the point estimates using the shift-share specification repre-sent larger impacts for both first generation and low income students. These resultsconfirm that the improvements in PFL mandates stem from a university’s exposureto PFLmandates rather than from transitory changes in student enrollment inducedby PFL mandates.

A.4.2 State-Level Difference-in-Differences for High In-state Universities

In this section, I abandon the use of the continuous treatment measure to esti-mate a more straight-forward difference-in-differences specification in which treat-ment status is assigned to each university at the state level. To isolate the sample toonly those that are most affected by the within-state adoption of a personal financeeducation mandate, I restrict the sample to public and private universities with ahistorically high in-state percentage of students. For each university, I calculate themean percentage of students who resided in the state in the previous year over thesample years and only include a university in this analysis if the mean percentageof in-state students is 70% or higher.45 The result is a sample of 656 universities ofwhich 370 are public and 286 are private. This subsample represents over 75%of the

45For the sample of universities, the median historical in-state percentage is 64% so this is roughlyhalf the universities in the main analysis

45

Figure A.3: Dose Response Shift-Share Estimates Relative to Baseline Specificationfor Public Universities

-4.1% -5.1%

-0.020

-0.010

0.000

0.010

0.020

OverallCohort

FirstGeneration

Low Income($0-$30k)

Middle Income($30k-$75k)

High Income($75k+)

Shift-Share Specification Baseline Specification

Default Rate

4.9%

1.3%

5.6%

1.3% 2.3%

4.4%

1.3%

5.0%

1.4% 2.1%

-0.050

-0.025

0.000

0.025

0.050

OverallCohort

FirstGeneration

Low Income($0-$30k)

Middle Income($30k-$75k)

High Income($75k+)

Shift-Share Specification Baseline Specification

Repayment Rate

The figure above plots a separate coefficient estimate and corresponding 95% confidence intervalwhere the independent variable is pfMandate and the outcome variable is denoted for each column.The estimates from the Shift-Share specification are reported with a square and the estimates fromthe baseline specification are replicated with a triangle. Proportional impacts are also printed to theright of each marker. The vector of control variables remains unchanged from the main specification.95% confidence intervals are constructed using standard errors clustered at the state level.

public universities in the sample but less than one-third of the private universities.In this specification, each university is assumed to only be affected by its own state’smandate adoption (if any) and universities in states that do not adopt a mandateact as controls. The specification is similar to Equation (4)

H8B ,C+6 = �pfMandateBC + �XBC + �B + �C + �8BC , (15)

where H8B ,C+6 is the same student loan repayment outcome for university 8 located instate B for the repayment cohort matched to high school graduating class C. Ratherthan pctBound8C as in Equation (4), pfMandateBC is equal to one if the state B hasa binding mandate for high school graduating cohort C. Also included are thevector of control variables XBC at the state level which include other course creditrequirements, high school staffing levels, availability of statemerit aid scholarships,and a vector of the state unemployment rates between periods C and C + 6. Fixedeffects for state (�B) and high school graduating cohorts (�C) are also included andstandard errors are clustered at the state level.

Table A.3 reports the estimated � coefficients for this specification for all uni-versities with 70% or higher historical in-state percentage for the main outcomevariable split by public and private universities. Columns 3 and 4 show improve-ments in the one-year repayment rate for first generation and low income students

46

Table A.3: Robustness: Difference-in-Differences for High In-state University Sam-ple

Default Rate Repayment Rate

(1) (2) (3) (4) (5) (6)Overall Overall First Gen Low

IncomeMiddleIncome

HighIncome

pfMandate -0.002 0.016 0.025** 0.024** 0.010 0.013(0.002) (0.010) (0.011) (0.010) (0.010) (0.011)

Universities 656 656 654 655 637 634Cohorts 1993-2006 2001-2008 2001-2008 2001-2008 2001-2008 2001-2008

Outcome Mean 0.045 0.586 0.546 0.469 0.626 0.727Percentage Effect -4.1% 2.7% 4.5% 5.1% 1.6% 1.8%

Regressions are weighted using the number of students used to compute each outcome metric. Eachcolumn reports a coefficient from a separate regression where the independent variable is pfMandate9Cand the outcome is denoted in the column header. The sample includes four-year universities with 70%or higher in-state share of students during the sample period. Default rate analysis includes high schoolgraduating classes 1993 through 2006 and repayment rate analysis includes high school graduating classes2001 through 2008 due to data availability. First Gen students are defined as students whose parentsdid not have a college degree. Low Income, Middle Income, and High Income students are defined ashousehold income less than 30,000, between 30,000 and 75,000 and above 75,000, respectively. Controlsinclude cohort weighted credit requirements in math, English, social studies, and science by high schoolgraduation cohort and controls for state level high school staffing, and availability ofmerit aid scholarships.Also included are university and high school graduation year fixed effects. Standard errors clustered atthe state level are presented in parenthesis. *** p<0.01, ** p<0.05, * p<0.1

similar to those found in Table 4. This suggests that the main findings are notsensitive to the continuous construction of pctBound.

A.4.3 Instrumenting for Enrollment Counts

As noted in Section 3, universities are required to send data on the previous stateof residence for each incoming cohort only in even numbered years. Universitiesmay elect to also provide this information in odd years but are not required. As aresult, the data containmanymissing values over the sample. Further, investigationof the data reveal numerous transcription errors in which the cohort is coded asincluding only students who graduated from high school longer than 12 monthsprior when this is highly unlikely given previous years’ data. In themain analysis, Ilinearly interpolate missing values using the neighboring non-missing years. How-ever, trends in attendance may not be linear in years and transitory shocks and timetrends in attendance numbers may occur which deviate from linearly interpolatedvalues.

In this section, I conduct a more thorough exercise to replace missing data thatuses more information to predict missing values by instrumenting enroll8B 9C withlinear and quadratic trends, a series of fixed effects, and the availability of statemerit aid scholarships. Equation (16) details the specification for this strategy:

47

enroll8B 9C =�8 + C · �8 + C2 · �8 + C · �B + C2 · �B+ C · �8 9 + C2 · �8 9 +meritAid9C +meritAid9C · {B = 9}+ � 9C + �8B 9C

(16)

In this specification, predicted values of enroll8B 9C are estimated by regressingenroll8B 9C on university fixed effects and state fixed effects both of which are in-teracted with linear and quadratic time trends. In addition, linear and quadratictrends for each university-by-feeder state are also included. I include an indicatorfor whether the feeder state offered a state merit aid scholarship for cohort C. Sincestate merit aid scholarships provide an added incentive to attend an in-state school,the addition of a scholarship might cause students to be less likely to attend anout-of-state school (Fitzpatrick and Jones, 2016). For this reason, I also include aninteraction of meritAid9C with an indicator for whether the feeder state is an in-stateuniversity since this effect would be opposite-signed. Lastly, I include feeder-state-specific year fixed effects to capture transitory shocks to feeder state level collegeenrollment.

I use the estimated coefficients andfixed effects to predict enroll8B 9C (�enroll8B 9C) forboth non-missing values included in the regression as well as missing observationsnot included in the regression. I then use �enroll8B 9C to construct �pctBound8BC asin Equation (3) to re-estimate Equation (4). Table A.4 presents the results fromthis exercise. The estimates are largely consistent with the estimates presented inTable 4.

48

Table A.4: Robustness: Dose Response Estimates with Instrumented Enrollment

Default Rate Repayment Rate

(1) (2) (3) (4) (5) (6)Overall Overall First Gen Low

IncomeMiddleIncome

HighIncome

pctBound -0.001 0.012 0.023** 0.023** 0.008 0.007(0.003) (0.008) (0.010) (0.010) (0.009) (0.009)

Universities 1,267 1,267 1,246 1,249 1,238 1,241Cohorts 1993-2006 2001-2008 2001-2008 2001-2008 2001-2008 2001-2008

Outcome Mean 0.042 0.596 0.539 0.460 0.633 0.750Percentage Effect -1.9% 2.0% 4.3% 4.9% 1.2% 0.9%

Regressions are weighted using the number of students used to compute each outcomemetric. Each column reportsa coefficient from a separate regression where the independent variable is �pctBound and the outcome is denoted inthe columnheader. The sample includes four-year universities. Default rate analysis includes high school graduatingclasses 1993 through 2006 and repayment rate analysis includes high school graduating classes 2001 through 2008due to data availability. First Gen students are defined as students whose parents did not have a college degree.Low Income, Middle Income, and High Income students are defined as household income less than 30,000, between30,000 and 75,000 and above 75,000, respectively. Controls include cohort weighted credit requirements in math,English, social studies, and science by high school graduation cohort and controls for state level high school staffing,and availability of merit aid scholarships. Also included are university and high school graduation year fixed effects.Standard errors clustered at the state level are presented in parenthesis. *** p<0.01, ** p<0.05, * p<0.1

A.5 Additional Tables and Figures

49

Figure A.4: Map of University Sample from College Scorecard

Public: 450Private: 936

The map above shows the locations and relative cohort sizes of the sample of public and privateuniversities. Each marker is weighted by the mean cohort size over the sample period. Someuniversities in the sample have missing GPS coordinates and are not plotted despite inclusion in thesample.

Figure A.5: Word Cloud of PFL State Standard Text

The image above shows a word cloud of the text for the state PFL standards for the following states:Arizona, Arkansas, Colorado, Florida, Georgia, Idaho, Iowa, Kansas, Louisana, Michigan, Missouri,New Hampshire, New Jersey, New York, North Carolina, Oregon, South Carolina, South Dakota,Tennessee, Texas, Utah, and Virginia.

50

Table A.5: Events per Academic Year

AcademicYear

Events Adopting States

1996 89 New York1997 01998 34 Michigan1999 02000 02001 02002 1 Wyoming2003 02004 02005 41 Arizona, Arkansas, Louisiana2006 10 South Dakota2007 130 Georgia, Idaho, North Carolina, Texas2008 6 Utah2009 38 Colorado, South Carolina2010 29 Missouri2011 68 Iowa, New Jersey, Tennessee2012 12 Kansas2013 13 Oregon2014 53 Florida, Virginia

Total 524

The table above details the number of university events in each aca-demic year where an event is defined as a year-over-year change inpctBound8BC of 50 percentage points or larger. In addition, the lastcolumn summarizes the states that adopt a personal finance man-date in each academic year. Events induced by New Hampshire’s1993 mandate occur before the sample period for outcome data.

51

Table A.6: Difference-in-Differences Estimates for Financial Literacy and Loan Lit-eracy from NPSAS

(1) (2) (3) (4) (5) (6) (7) (8)FL1: FL2: FL3: FL: LL1: LL2: LL3: LL:

Interest Inflation Risk NumCor-rect

Credit GarnishWages

TaxRe-turns

NumCor-rect

pfMandate 0.004 -0.002 0.002 0.004 0.013 0.033** 0.018 0.064**(0.020) (0.011) (0.019) (0.040) (0.015) (0.015) (0.016) (0.030)

Observations 45,230 45,230 45,230 45,230 45,230 45,230 45,230 45,230Cohorts 2009-

20162009-2016

2009-2016

2009-2016

2009-2016

2009-2016

2009-2016

2009-2016

Outcome Mean 0.662 0.856 0.466 1.944 0.753 0.558 0.660 1.97Percentage Effect 0.5% -0.4% 0.2% 0.1% 1.7% 6.0% 2.7% 3.2%

Source: U.S Department of Education, National Center for Education Statistics, Restricted-use National Post-secondary Student Aid Study 2016. Each column reports the coefficient of the binary personal finance mandatevariable from a separate linear regression. Columns 1-3 and 5-7 report the impact of a personal financemandateon an indicator variable for whether the respondent correctly answered the question from a linear probabilitymodel. Columns 4 and 8 show the impact of the mandate on the total number of correct questions answered.Each regression includes controls for race, gender, Expected Family Contribution, year of schooling, and publicor private high school attended. Also included are state of high school attendance and high school graduationyear fixed effects. Standard errors are clustered at the state level. *** p<0.01, ** p<0.05, * p<0.1

TableA.7: Question Text for Financial Literacy and Student LoanLiteracyQuestions

Label Question Text Choices

FL1: Interest Imagine that the interest rate on your savings account was 1% per year and inflation was 2% per year. After1 year, how much would you be able to buy with the money in this account?

More than todayExactly the sameLess than today

FL2: Inflation Suppose you had $100 in a savings account and the interest was 2% per year. After 5 years, how much doyou think you would have in the account if you left the money to grow?

More than $102Exactly $102Less than $102

FL3: Risk Buying a single company’s stock usually provides a safer return than a stock mutual fund. TrueFalse

LL1: Credit If a borrower is unable to repay his or her federal student loan, the government can report that the studentdebt is past due to the credit bureaus

TrueFalse

LL2: GarnishWages

If a borrower is unable to repay his or her federal student loan, the government can have the student’semployer withhold money from his or her pay (garnish wages) until the debt, plus any interest and fees, isrepaid

TrueFalse

LL3: Tax Re-turns

If a borrower is unable to repay his or her federal student loan, the government can retain tax refunds andSocial Security payments until the debt, plus any interest and fees, is repaid

TrueFalse

52