Student Loans and Homeownership

A.  Institutional Background

Student loans are a popular way for Americans to pay the cost of college, and the use of such loans has been increasing in recent years. In 2005, 30% of 22-year-olds had accumulated some student loan debt, with an average real balance among debt holders of approximately $13,000. By 2014, these numbers had increased to 45% and $16,000, respectively.⁵

The vast majority of students have access to federal student loans, which generally do not involve underwriting and can charge below-market rates.⁶ The amount of such loans students can borrow is capped by Congress, however. Federal student loans are also not dischargeable in bankruptcy, reducing the options of borrowers in financial distress. Student borrowers frequently exhaust their available federal loans before moving on to generally more expensive private loans, often with a parent as cosigner. Historically, the typical student loan is fully amortizing over a 10-year term with fixed payments. Deferments and forbearances can extend this term, as can enrollment in alternative repayment plans, such as the extended repayment plan (available for borrowers with high balances) and income-driven repayment plans (which have become more common in recent years and are available for borrowers with elevated debt-to-income ratios), and through loan consolidation.

Student loan debt can impose a significant financial burden on some borrowers. Despite the inability to discharge federal loans through bankruptcy, 16% of recipients with outstanding federal student debt were in default as of March 2017 (Baum et al. 2017). Student borrowers are often young and at a low point in their life-cycle earnings profile. The financial difficulties may be more severe for students who fail to graduate. Of the federal student loan borrowers who entered repayment in 2011–12 without a degree, 24% defaulted within 2 years.⁷

B.  Theoretical Mechanism

We conjecture that three underwriting factors provide a channel through which student loan debt can affect the borrower’s ability to obtain a mortgage and, hence, enter homeownership.⁸ First, a higher student loan debt payment affects the individual’s ability to accumulate financial wealth that can then be used as a source of down payment. Second, a higher student loan payment increases the individual’s debt-to-income (DTI) ratio, potentially making it more difficult for the borrower to qualify for a mortgage loan. Third, student loan payments can affect the borrower’s credit score. On the one hand, the effect can be positive: timely payments of student loan debt may help borrowers to improve their credit profiles. On the other hand, potential delinquencies adversely affect credit scores, thereby hampering borrowers’ access to mortgage credit. At the same time, other nonunderwriting factors might have effects as well. For example, from a behavioral perspective, if individuals exhibit debt aversion and wish to repay at least some of their existing debt prior to taking on new debt in the form of a mortgage, larger student loan debt burdens can further delay their entry into homeownership. Available evidence points to the existence of debt aversion in different settings, suggesting that this mechanism might play a role in reducing the probability of homeownership (see, e.g., Loewenstein and Thaler 1989; Thaler 1990; Field 2009; Palameta and Voyer 2010; Rothstein and Rouse 2011).

Various factors might influence how the effect of student loan debt on homeownership changes in the years after leaving school. Since cumulative balances are generally largest immediately on entering repayment (see fig. 15 in Looney and Yannelis 2015), there are at least four reasons to believe that the ceteris paribus effect of higher student loan debt on homeownership access might be largest immediately on school exit. First, given that the income profile tends to rise over the life cycle and student loan payments are fixed, the DTI constraint should ease over time, as should the budget constraint, thereby allowing the individual to potentially accumulate assets for a down payment at a faster rate. Second, once all debt is repaid, the student loan debt component of debt payments in the DTI constraint disappears entirely. Of course, the past effects of student loan payments on accumulated assets are likely to be more persistent if student loan payments significantly impaired the individual’s ability to save at a rate comparable to that of an individual with less student debt for a period of time. Third, the Fair Credit Reporting Act prohibits the credit bureaus from reporting delinquencies more than 7 years old, so any difficulties the borrower had meeting payments will eventually drop off her credit report. Last, any effect of debt aversion induced by a higher student loan debt burden at school exit should diminish over time as the balance is paid down. We articulate these mechanisms more formally in a model presented in the appendix.

While our discussion thus far suggests that the effect of student loan debt on homeownership attenuates over time due to student loan debt repayment and rising incomes, there may be countervailing effects. In particular, the propensity for homeownership is generally relatively low among those newly out of school and increases with age. Hence, the number of marginal home buyers may peak many years after school exit, suggesting that the effect of student loan debt might be increasing as the debtor ages. Also, individuals may exhibit habit formation in their housing tenure choice. A marginal home buyer who is induced into renting by her debts may become accustomed to renting, in which case the apparent effect of student loan debt on homeownership could persist for many years.

The average marginal effect of student loan debt on homeownership for any given population will depend on the density of individuals near the relevant mortgage underwriting thresholds. These underwriting criteria can change over time as mortgage credit availability eases and tightens. This paper investigates a population of individuals who were mostly making their home-buying choices prior to the housing market collapse of the late 2000s. Mortgage credit tightened considerably in the following years and has subsequently been (slowly) relaxing. The average marginal effect of student loan debt may therefore be different in years with considerably different levels of credit availability, an important point to keep in mind when extrapolating our results to other time periods.

The mechanisms discussed in this section are not specific to student loan debt—auto loans and credit card debt could impose similar burdens on debtors in the housing market. Student loan debt is particularly interesting to study, however, because of the ease of availability of student loads. Young people without incomes or collateral are able to take on tens of thousands of dollars of debt to pay for their education without any underwriting of the loans. In contrast, a borrower without a credit history or source of income would face very tight limits in markets for privately provided credit. Student loans therefore present a unique channel for individuals to become heavily indebted at a young age. See section IV.D for an empirical treatment of the effects of total nonhousing consumer debts.

A.  Patterns of Debt and Homeownership

Student loan debt is correlated with homeownership, but this relationship is not stable over the life cycle. Figure 1 plots the probability of ever having taken on a mortgage loan against the individual’s age for different levels of student debt. In figure 1A, we compare individuals who attended college before age 23 without taking on debt with those who did borrow as well as with individuals who did not attend college by that age. Debt-free college attendees have a higher homeownership rate than their indebted peers at age 22, but those with debt catch and surpass the debt-free group by age 29. In figure 1B, we refine college attendees into three categories based on amount borrowed: no borrowing, less than $15,000, and more than $15,000. Students who borrow moderate amounts start off less likely to own than nonborrowers but eventually catch up. Those who borrowed the most start with the lowest homeownership rate at age 22 but are substantially more likely to be homeowners by age 32 (the median age of first home buying, according to the National Association of Realtors). From these plots one might be tempted to conclude that, at least in the medium run, higher student loan debt leads to a higher homeownership rate.

Determining how student loan debt affects homeownership is not so straightforward, however. Individuals with differing amounts of student loan debt may also differ in other important ways. Notably, they may have different levels of education, which is itself highly correlated with homeownership (possibly through an effect on income). Figure 1C restricts the sample to individuals who attained a bachelor’s degree before age 23. Within this group, those without student loan debt always have a higher homeownership rate than borrowers. Comparing the bottom two panels, students who borrowed more than $15,000 had the highest homeownership rate among the general college-going population after age 27 but have the lowest rate among the subset with a bachelor’s degree at all ages. Bachelor’s degree recipients with no student loan debt have the highest homeownership rate across the range of ages. As such, simple correlations clearly do not capture the whole picture.

B.  Selection on Observables

Further factors that are correlated with both student loan debt and homeownership (and may be driving the observed relationship between these two variables of primary interest) include the type of school attended, choice of major, and local economic conditions, for example. One potential identification strategy is to attempt to absorb all of these potential confounders with an extensive set of control variables. For the purpose of comparison with our instrumental variable estimates (presented in sec. IV.D), we run age-specific regressions of an indicator for homeownership on student loan debts and various sets of controls using a probit model. In these and subsequent regressions, the individual-level explanatory variables (including student loans disbursed) are all measured at the end of the individual’s 22nd year. All standard errors are clustered at the home state level.

Estimates of the effect of student loan debt on homeownership by age 26 are presented in Table 2. Marginal probabilities, averaged over all individuals in the sample, are shown. Estimates are generally similar across the range of specifications in columns 1–4, which sequentially control for an increasingly rich set of covariates, including school sector, degree attained, college major, Pell Grant receipt, state and cohort fixed effects, and, finally, state-by-cohort fixed effects. A $1,000 increase in student loans disbursed before age 23 is associated with an approximate 0.1 percentage point reduced probability of homeownership by age 26. Figure 2 plots estimates of the marginal effect of student loan debt against borrower’s age, derived from the regressions using the vector of controls in column 5 of Table 2. The estimated effect starts negative for borrowers in their early 20s and becomes positive when they reach their early 30s.

Our estimates from these selection-on-observables regressions are closely in line with previous findings in the literature. Using the National Longitudinal Survey of Youth 1997, Houle and Berger (2015) estimate that a $1,000 increase in student loan debt decreases the probability of homeownership by 0.08 percentage points among a population composed largely of 20- and 25-year-olds. Similarly, using the National Education Longitudinal Study of 1988, Cooper and Wang (2014) find that a 10% increase in student loan debt (approximately equivalent to a $1,000 increase for our sample) reduces homeownership by 0.1 percentage points among 25- and 26-year-olds who had attended college.

C.  Instrumental Variable Estimation

While the estimators used above control for some important covariates, there may still be unobservable variables biasing the results. It is not clear, a priori, in which direction the estimates are likely to be biased by such unobservable factors. For example, students with higher unobservable academic ability may borrow more, either because they choose to attend more expensive institutions or because they anticipate greater future incomes. These higher-ability students would also be more likely to subsequently become homeowners, introducing a positive bias in the estimates. Conversely, students from wealthy backgrounds may receive financial assistance from their parents and therefore need to borrow less to pay for school than their less advantaged peers. For example, Lovenheim (2011) finds shocks to housing wealth affect the probability families send their children to college. Parental contributions could help these same students to later purchase a home, which would tend to introduce a negative bias. The covariates we have may not adequately control for these or other omitted factors. Reverse causality is also a potential source of bias if purchasing a home before leaving school affects students’ subsequent borrowing behavior. To reliably identify the causal effect of student loan debt, we need a source of variation that is exogenous to all other determinants of homeownership.

We propose that the average tuition paid by in-state students at public 4-year universities in the subject’s home state during his or her prime college-going years provides quasi-experimental variation in eventual student loan balances for students who attended those schools. A large fraction of students attend public universities in their home state, so the loan amounts they require to cover costs vary directly with this price (in our sample, nearly half of the students who had attended any college before age 23 had attended a public 4-year university in their home state). Additionally, this tuition cannot be affected by the choice of any particular individual. Rather, changes in the tuition rate depend on a number of factors that are arguably exogenous to the individual homeownership decision, ranging from the level of state and local appropriations to expenditure decisions by the state universities.

A short overview of the major drivers of prevailing tuition rates will help clarify the validity argument and locate potential points of failure. One major source of tuition increases is changes to particular schools’ cost structures. According to Weeden (2015), these costs include compensation increases for faculty members, the decision to hire more administrators, benefit increases, lower teaching loads, energy prices, debt service, and efforts to improve institutional rankings, all of which have been linked to tuition increases since the 1980s. Institutions also compete for students, especially those of higher academic ability, by purchasing upgrades to amenities such as recreational facilities and residence halls. These upgrades are often associated with increased tuition to pay for construction and operation of new facilities. Finally, tuition and fees are frequently used to subsidized intercollegiate athletic ventures. In recent years, athletic expenses have increased and now may require larger subsidies from tuition and fee revenue at many colleges.

Another major driver of tuition rates is the level of taxpayer support. As described in Goodman and Henriques (2015) and Weerts, Sanford, and Reinert (2012), public universities receive a large portion of their operating income from state and local appropriations. The amount of state and local revenue that public colleges receive is itself influenced by a diverse set of factors that weigh on legislators in allocating funds, including state economic health, state spending priorities, and political support for affordable postsecondary education. Since public colleges can, in theory, offset the lost revenue from appropriations with increased tuition, appropriations for higher education can be crowded out by funding for other state programs.

Any correlation between the tuition charged at public universities and state-level economic conditions (through the effect of economic conditions on appropriations) raises a concern about the validity of tuition as an instrument. To address this potential source of bias, we split our sample into treatment and control groups, with the treatment group defined as the individuals who attended a public 4-year university before they turned 23. We then compare the outcomes in the treatment group to those in the control group, which consists of all other individuals (except in specifications shows in col. 7 of Table 4, where the control group is all other individuals with at least some postsecondary education before age 23). Treatment group subjects pay the tuition charged at public 4-year universities, so their total borrowing before turning 23 is directly affected by this tuition. In contrast, the control group is not directly affected by the tuition at public 4-year universities (which they did not attend). Our instrument is therefore the interaction between the tuition charged at public 4-year universities and an indicator for membership in the treatment group. This framework therefore allows us to control for any correlations between state-level shocks and tuition rates—either by including tuition rates directly as a control variable or by using state-by-year fixed effects—with the homeownership rate of the control group absorbing unobserved variation in economic conditions. We devote further consideration to the potential endogeneity of tuition in section IV.E.

A further concern might be that changes in tuition reflect other channels not absorbed by the control group, such as changes in school quality, and hence students’ later economic outcomes. However, we can exploit a difference in the source of tuition funds to test for bias along these lines. Specifically, the findings of Belley, Frenette, and Lochner (2014) suggest that the net tuition paid by lower-income students is less strongly linked to the sticker price due to the availability of need-based grants. Our data allow us to further refine the treatment group into those who did not receive any federal need-based aid in the form of Pell Grants (and whose student loan borrowing therefore varied more closely with the tuition rate) and those who did receive such aid before age 23. Estimates of the effect of tuition on these latter students’ subsequent homeownership provides a placebo test for the instrument—students who receive Pell Grants experience the same changes in school and economic environment as their peers without Pell Grants but are not exposed to the same variation in debt. We will demonstrate a strong effect of the tuition charged at public 4-year universities on the student loan borrowing and subsequent homeownership only of students who did not receive any Pell Grant aid. We will find little evidence that tuition affects student loan borrowing or homeownership for students who did receive Pell Grants. The absence of any negative effect on their homeownership rates suggests that variation in school quality (or other state-level factors specific to the treatment group) are not biasing our main results away from zero. We discuss these results in detail in section IV.E.

We model the probability of individual i becoming a homeowner by age t using equation (1):

We deal with the endogeneity of student loan debt by estimating a first stage in which X_i is modeled using equation (2):

The parameter β₂ captures any partial correlation between tuition rates and homeownership among the control group, absorbing any state-level shocks that affect both tuition and the homeownership rate. Note that in specifications with state-by-year fixed effects β₂ is not identified, as the average tuition rate is collinear with the fixed effects. The parameter β₃ captures the average difference in homeownership rates between the treatment and control groups. We are left identifying β₁, the effect of student loan debt on homeownership, by the widening or shrinking of the gap in homeownership rates between public 4-year school attendees and the general population as tuition rates change, analogous to a difference-in-differences estimator.

Estimates of β₁ may be inconsistent if membership in the treatment group is influenced by tuition rates. In particular, if the attendance decisions of students considering public 4-year universities are swayed by the prevailing tuition, then our estimates would suffer from sample selection bias. However, we will show that the variation in tuition exploited in this study exert no meaningful effect on the probability of a student attending a public 4-year university. Given this result, we believe it is reasonable to consider treatment group membership to be exogenous. The issue of selection into the treatment group is discussed further in section IV.F, in which we also consider the potential endogeneity of other educational outcomes. In particular, we show that Pell Grant receipt is not affected by changes in tuition.

The treatment group consists of traditional students—those who entered college immediately or very soon after high school and attended a public 4-year university. Care should be taken when extrapolating our results to the general population, which includes many individuals who enrolled in a private or public 2-year university or who first attended college later in life. If such individuals respond to debt much differently than traditional students, we do not capture this heterogeneity of treatment effect in our estimates.

D.  Instrumental Variable Estimation Results

First-stage results from regressing student debt on the instrument and other controls are presented in Table 3. Across specifications, a $1,000 increase in the sum of average tuition across the 4 years after the individual turned 18 is associated with an approximately $150 increase in student loan debt for students in the treatment group. The estimates are strongly statistically significant, with F-statistics far exceeding typical rule-of-thumb thresholds for linear models in all our specifications except column 1 (which does not include any control variables) and column 7 (which drops anyone who did not attend college from the control group). For reference, after controlling for state and cohort fixed effects, the residual of the 4-year sum of in-state tuition has a standard deviation of $915 across our sample.

Turning now to the second stage, we find a considerably larger effect, in absolute terms, of student loan debt on homeownership than in the earlier specifications without the instrument. We present the results for the effect on homeownership at age 26 for a variety of specifications in Table 4. Across specifications, we find a $1,000 increase in student loan debt leading to an approximate 1–2 percentage point decrease in the probability of homeownership. Since the average treatment group student in our sample had accrued, in constant 2014 dollars, approximately $10,000 of federal student loan debt before age 23, the $1,000 increase in student loan balances represents an approximate 10% increase in borrowing for the average person in the treatment group. Further interpretation of the magnitude of these results is presented in section V.

Figure 3 plots estimates of the marginal effect of student loan debt against the borrower’s age for several different specifications, along with 95% and 90% confidence intervals robust to clustering at the home state level. While the estimated magnitude of the effect of student loan debt is fairly consistent across specifications through student’s mid-20s to late 20s, statistical significance varies. In our most restrictive specification, using state-by-cohort fixed effects, we cannot reject the null hypothesis (that student loan debt has no effect on homeownership) at conventional significance levels (fig. 3B). However, after discarding students who received Pell Grants (a subgroup whose debt should be less influenced by the instrument), we can reject the null at 10% confidence levels at every year but one from ages 24–31, even with the full set of fixed effects (fig. 3C).

The estimates from the instrumental variable specifications imply a considerably stronger effect than those from the selection-on-observables estimates in section IV.B. This difference suggests the presence of unobservable factors biasing the latter estimates. In particular, individuals with greater levels of student loan debt are positively selected into homeownership—that is, they have a greater underlying (unobservable) propensity to become homeowners than individuals with smaller amounts of debt do. It may be, for example, that students with greater labor market ability take on more student loan debt, either as a result of attending more expensive schools or because they anticipate higher lifetime incomes. These high-ability (and highly indebted) individuals are then also more likely to become homeowners in their mid-20s.

In our preferred specification we include controls for educational outcomes (specifically school sector, degree attained, and major choice) because these covariates could affect earnings and homeownership conditional on tuition. Failing to control for these outcomes could therefore bias our estimates of the relationship between tuition and homeownership. However, it may also be possible that these outcomes are affected by tuition. As such, controlling for them could then introduce a different bias (although we would not expect tuition at public 4-year schools to have much effect on some of the covariates, such as the choice between all other education sectors). We therefore show specifications both with and without these controls (compare cols. 1 and 2 of Table 4). The results are broadly similar regardless of whether education controls are included, so neither source of bias seems to be of much concern. In section IV.F we show that there is little evidence that our measured educational outcomes are affected by movements in tuition.

It is worth keeping in mind that tuition changes could affect homeownership via channels not directly measured by student loan debt. If students (or their parents) have assets they draw down to pay for college, a higher tuition leaves them with less left over for an eventual down payment on a house. This behavior would tend to bias our estimates of the effect of debt away from zero.

Stripping away the assumed channel of student loan debt, we can look directly at the reduced-form effect of tuition on homeownership for the treatment and control groups. Table 5 presents results of regressing homeownership directly on the instrument and usual vectors of controls. Looking across the columns, every additional $1,000 of tuition (charged over a 4-year period) leads to a 0.2–0.4 percentage point lower homeownership rate for the treatment group at age 26. In contrast, as illustrated in columns 1–4, tuition does not appear to be negatively correlated with homeownership for the control group.

It is not surprising that the reduced-form effect of tuition is considerably smaller than the estimated effect of debt. Debts do not rise one-for-one with tuition hikes, for several reasons. First, not all students attend school full time for four straight years after high school. On average, individuals in our treatment group were enrolled at a public 4-year university for 570 days in the 4 years following their eighteenth birthday—approximately half of the potential school days, excluding summer and winter breaks. Furthermore, according to the Digest of Education Statistics, approximately 30% of undergraduates at public 4-year universities were attending only part time during the 1990s (the relevant time period for our sample). Second, not all students pay the sticker price of tuition. For example, many students receive scholarships or need-based grants. Based on annual national averages over the period 1997–2017 (using data from Ma et al. 2017), every $1,000 increase in real posted tuition at public 4-year universities was associated with a $350 increase in the net price paid by their students. For all these reasons, imposing an additional $1,000 of debt on students would likely affect their homeownership rate more than the 0.2–0.4 percentage points estimated in the reduced-form specification. Third, students may pay for some increases in the remaining net cost of college through methods other than borrowing—for example, work study or reducing consumption—further reducing the pass-through of sticker-price tuition to student loan debt. As we showed in Table 3, about $150 of every $1,000 increase in tuition passes through to students’ debt.

As we discuss in section II.B, student loan debt is unique in its availability to young people with poor credit or no credit history. That said, other debts could affect homeownership similarly, through many of the same channels that we discuss in that section. Ideally, we would like to capture the responses of students’ entire debt portfolios—not only their federal student loans—to changes in tuition. However, the timing of data collection presents an obstacle to estimating the effect of total debt—credit bureau data are available only biennially, so we are able to observe debt before age 23 for only a subset of individuals in our data. Additionally, the oldest cohort was already 23 years old in 1997, the first year credit bureau data are available to us. Because of these features of the credit bureau data, we cannot create consistent measures of total debt by age for everyone in our sample. In contrast, the student loan data from NSLDS that are merged on our core credit bureau sample provides a complete history of each subject’s federal student loan borrowing, as it also spans the period prior to 1997.

Despite these data limitations, when we ran estimates using total nonmortgage debt (measured at age 23 or 24, with the estimation sample restricted to the population for whom these data were available) as the endogenous variable, we get similar results of the effect of the marginal dollar of debt on homeownership.¹⁶ The full tables of results for our various specifications are presented in the appendix. The first stage is somewhat stronger, with a $1,000 increase in tuition causing an additional $200 to $350 dollars in total debt, as opposed to a range of about $100 to $200 in Table 3. In the second stage, estimates are somewhat attenuated relative to those in Table 4. Using the specification from column 6, we estimate that a $1,000 increase in total debt reduces the probability of homeownership by 1.2 percentage points at age 26, while this figure was 1.75 percentage points for our main results using federal student loan debt records.

E.  Endogeneity of Tuition

Our identifying assumption that the instrument is exogenous to unobserved determinants of homeownership is not directly testable. We can, however, test for some plausible sources of endogeneity. For example, in-state tuition rates may be correlated with local housing and labor market conditions, which in turn affect homeownership rates. To see that such omitted variables are unlikely to bias our estimates, compare the estimates across columns 3–5 in Table 4. Column 4 differs from column 3 by the inclusion of yearly home state–level economic controls: namely, the unemployment rate, log of average weekly wages, and the CoreLogic house price index, all measured in the subject’s home state at the age of 22. The estimated coefficient on student loan debt is stable across columns 3 and 4, suggesting that these local economic conditions are not driving the results. Furthermore, column 5 includes home state–by–cohort fixed effects that should absorb the effects of all broad economic conditions at the state level. Again, the coefficient of interest is quite stable to this stricter set of controls, suggesting that our findings are not substantially biased by market-level factors.

Further evidence that tuition affects homeownership only through the student loan channel is provided by the absence of any clear effect of tuition on the control group. The estimated coefficient on tuition, which measures the partial effect on the control group’s homeownership rate, is small and changes sign across specifications. This can be seen by comparing columns 1–4 of Table 5. Since control group individuals do not pay tuition at public 4-year universities, their homeownership rates should not be correlated with that tuition except through omitted-variable bias. We find no evidence that such omitted variables are affecting the correlations between tuition and homeownership. This is essentially a placebo test, validating the contention that we are picking up an effect of tuition rather than the influence of some unobservable factor correlated with it.

We may still be concerned that the correlation between tuition and homeownership among the treatment group is being driven by factors specific to public 4-year universities, such as school quality. As we outlined in section IV.C, we run another placebo test to directly check this concern. The test is motivated by Belley, Frenette, and Lochner (2014), whose findings suggest that the net tuition paid by lower-income students is less strongly tied to the sticker price due to the availability of need-based grants. While we do not observe family income in our data, we do observe Pell Grant receipt. We split the sample into those individuals who did and did not receive any Pell Grant aid before they turned 23. The former group received need-based aid, so their student debt burden should be less influenced by variation in the average in-state charged tuition. We have shown above that tuition is strongly relevant in explaining student loan debts among the treatment group in the non-Pell population (see Table 3). In contrast, the estimated first stage is smaller by half and not statistically significant for the population who received Pell Grant aid (results not shown, available on request).

Given the weak first stage, finding a reduced-form effect of tuition on the homeownership of Pell Grant recipients in the treatment group would suggest that the exclusion restriction is violated. The estimated reduced-form effect of the tuition instrument on homeownership for the population that received Pell Grants is shown in column 8 of Table 5. Reassuringly, we do not find a significant effect of tuition at public 4-year universities on homeownership for this population. In fact, the estimated (placebo) effect is actually positive, although not significant. This finding further suggests that the negative correlation between the tuition measure and homeownership in our preferred specification is causal. Taking the point estimates for the Pell recipient group seriously, however, this test might suggest that our main estimates are biased toward zero, and we are somewhat underestimating the true effect of student loan debt on homeownership.

As constructed, our control group includes individuals who never attended college as well as students at private schools and public 2-year schools. A potential critique of the exclusion restriction is that tuition rates may reflect economic conditions relevant for college-goers but not for their peers who did not receive any postsecondary education. If such were the case, our estimates may still be biased by the endogeneity of tuition to college attendee-specific economic shocks, despite the evidence discussed above. We deal with this issue by dropping all observations for those who had not enrolled in college before age 23 from the sample and reestimating equations (2) and (1) on the subpopulation with at least some college education. Results are presented in column 7 of Table 4. The estimated effect of student loan debt on homeownership is quite similar to that from previous specifications despite the redefined control group.

F.  Endogeneity of Educational Outcomes

A further potential issue is bias from sample selection due to the possibility that tuition rates may affect the relationship between debt and homeownership through the composition of the student population at public 4-year universities. Higher tuition may deter some students from attending these schools. If such students have notably different propensities to become homeowners than inframarginal students, then our estimates of the effects of debt on homeownership would be biased. However, note that while the homeownership rate of the treatment group falls substantially when tuition rises, this is not matched by an increase in the homeownership rate of the control group. The control group has a lower homeownership rate than the treatment group, so if individuals with a higher than average propensity to become homeowners switch out of the treatment group, then we would expect a significant increase in the control group’s homeownership rate. As previously mentioned, columns 1–4 of Table 5 show that the estimated effect of tuition on the homeownership of the control group is small, statistically insignificant, and changes sign across specifications.

To further address this potential source of bias, we can test whether our tuition measure affects students’ decisions to attend a public 4-year university. If variation in the average in-state tuition is not correlated with enrollment decisions, then endogenous selection into the treatment group is not a concern.

In column 1 of Table 6, we show the results of regressing D_i—the indicator for having attended a public 4-year university before age 23—on our tuition measure and state and cohort dummy variables. We find no evidence that changing tuition affects the probability that an individual attends such a school. For completeness, in column 2 we show the estimated effect of tuition on the probability of college attendance regardless of sector, for which we find a similar null result. In column 6, we restrict the sample to only those who attended college before age 23 and again find no significant effect of tuition on the probability of attending a public 4-year university. This last test suggests that tuition at public 4-year universities does not induce switching between school sectors, at least for the relatively modest variation in the cost of schooling that our study exploits. Given this evidence, we believe that defining our treatment group based on attendance at a public 4-year university does not meaningfully bias our estimates.

Previous studies have reached mixed conclusions as to the effect of tuition on college attendance. Similar to our estimates, Shao (2015) and Bleemer et al. (2017) use variation in tuition at public institutions to conclude the attendance and completion margins, respectively, are insensitive to costs. Other studies have found more significant effects. As discussed in a review paper by Deming and Dynarski (2010), this literature often focuses on low-income or generally disadvantaged students, and the best identified papers find a $1,000 tuition increase (in 2003 dollars) reduces enrollment by 3–4 percentage points. These various findings may be reconcilable if the decision of traditional students to attend public 4-year colleges is price inelastic, while the attendance decision of marginal students considering community colleges or certificate programs is more price sensitive (Denning 2017).¹⁷

We can test for this potential heterogeneity in price elasticity by regressing the probability of attending a public 2-year college against the average tuition charged by such schools in the individual’s home state in the 2 years after they turned 18. Results of these regressions are shown in column 3 of Table 6. This test is analogous to our baseline experiment, shown in column 1 of Table 6. Although not statistically significant, the point estimate of the effect of public 2-year tuition on enrollment at public 2-year colleges is substantially larger than the point estimate on the effect of public 4-year tuition on attendance at public 4-year universities. Specifically, a $1,000 tuition increase (in 2014 dollars) decreases public 2-year college attendance by more than 2 percentage points. This effect, although imprecisely estimated, is quite similar in magnitude to previous estimates covered in Deming and Dynarski (2010), especially when correcting for the 28 percentage points of inflation between 2003 and 2014.

Tuition may also affect other educational outcomes, such as degree completion, take up of financial aid, or the choice of major. These outcomes may in turn affect the probability of homeownership—for example, completing a college degree may boost the student’s income and allow him or her to afford a home—which would violate the exclusion restriction. We therefore control for these outcomes in our preferred specifications. However, such outcomes may be endogenous to unobservable determinants of homeownership, in which case the estimator would still be inconsistent. Comparing columns 1 and 2 of Table 4, we can see that the estimated effect of student loan debt on homeownership is qualitatively similar regardless of whether additional educational controls are included. We can also test for whether tuition is correlated with any of these outcomes. In columns 4 and 7 of Table 6, we present estimates of the effect of tuition on the probability of completing a bachelor’s degree before age 23 for the general population and for the subsample that attended college, respectively. We do not find any significant correlation between tuition and the completion of a bachelor’s degree. In columns 5 and 8, we estimate the effect of tuition on the probability of receiving any federal Pell Grants for the full sample and the college-going subsample. Again, the estimated effect is very small and not significant.

Finally, we estimate the effect of tuition on the choice of major for those attending a public 4-year school before age 23, modeled as a multinomial logit regression with majors categorized into one of 16 groups. Results are presented in Table 7. We find little evidence of an effect of tuition on major choice. The estimated effect on the risk ratio relative to no declared major is significant for only one major choice: public administration and social work (number 13). This major choice is quite uncommon as well; only 42 individuals in our treatment group sample majored in this field.

G.  Additional Outcomes

As we discussed in section II.B, there are multiple channels by which student loans could theoretically affect homeownership. One such channel we hypothesize is the detrimental effect of student loan debt on the borrower’s credit score.¹⁸ Increased debt balances could worsen credit scores directly if the credit score algorithm places a negative weight on higher student debt levels.¹⁹ Moreover, increased debt could lead to delinquencies that would have a further derogatory effect. Delinquencies are a salient concern for many student loan borrowers—according to a report by the Federal Reserve Bank of New York (FRBNY), the fraction of student loan balances that were 90 days delinquent or more increased from more than 6% in 2004 to more than 11% in 2017 (FRBNY 2018). The sign of the overall effect is ambiguous, however, as taking out and subsequently repaying student loans may help some borrowers establish a good credit history and thus improve their scores.

We estimate the effect of student loan debt on credit scores, regressing the probability that a borrower’s credit score ever fell below one of two underwriting thresholds by a given age against their student loan debt and the usual vector of controls. We use the same instrumental variable strategy as in section IV.C to deal with the endogeneity of student loan debt. The thresholds are chosen to roughly correspond to FICO scores of 620 and 680.²⁰ We refer to the lower credit range as “subprime” and to the intermediate range as “nonprime.” Results from the full sample for age 26 are presented in columns 1 and 3 of Table 8, with the specification corresponding to column 5 of Table 4. Columns 2 and 4 present the results of the regressions for the subsample that did not receive any Pell Grant aid before age 23, with the specification corresponding to column 6 of Table 4. Results are similar for both the full sample and the restricted subsample, suggesting that a $1,000 increase in student loan debt causes a nearly 2 percentage point increase in the probability a borrower falls below each of the thresholds, although the estimates are slightly more precise for the group that did not receive any Pell Grant aid. It appears that student loan debt plays a role in driving down borrower’s credit scores.

In columns 5 and 6, we report the estimated effect of student loan debt on the probability of ever having been 90 days delinquent or more on a student loan payment for the full sample and restricted subsample. The results suggest that a $1,000 increase in debt increases the probability of ever having been 90 days delinquent or more by age 26 by 0.3 and 0.5 percentage points, respectively. The estimate for the non-Pell recipient population is larger and more precise. These results may suggest that borrowers are more likely to miss payments when their debt burdens are greater and the resulting damage to their credit scores makes qualifying for a mortgage more difficult. In columns 7 and 8 we show the estimated effect of student loan debt on borrowers becoming delinquent on credit card debts or auto loans. Together, mortgages, student loans, auto loans, and credit card balances account for more than 96% of all household debt (authors’ calculations based on credit bureau data from the FRBNY Consumer Credit Panel/Equifax). In neither sample do we find evidence that increased student loan debt leads to more delinquencies on these other forms of debt.

In figure 4 we plot the estimated effect of student loan debt on having a nonprime credit score (corresponding to a FICO score of 680 or below) and on ever having been 90 days delinquent or more on a student loan payment, by age, from 22 to 32. Results for both the full sample (fig. 4A, 4B) and the subsample without any Pell Grant aid (fig. 4C, 4D) are shown. The estimated effects on credit scores, shown in figure 4A and 4C, are not significant at first but grow in magnitude and remain persistently significant after age 26 for both samples. In figure 4B and 4D, we can see a similar pattern for the effect of student loan debt on delinquencies, although the estimates are only significant across multiple years for the subsample that did not receive Pell Grants. These results suggest that access to homeownership could be impaired by student loan debt’s negative effect on credit scores, in part through the channel of increasing delinquencies on those debts. However, because student loan debt begins to have a significant effect on both homeownership and credit scores at about the same age, we cannot rule out the possibility of reverse causality (i.e., that mortgage debt improves credit scores).