Does Federal Financial Aid Affect College Enrollment?
Evidence from Drug Offenders and the Higher Education Act of 1998

Michael F. Lovenheim 1
Emily G. Owens 2
February 2012

Abstract
In 2001, amendments to the Higher Education Act made people convicted of drug offenses ineligible for
Federal financial aid for up to two years prior to their conviction. Using rich data on educational
outcomes and drug charges in the NLSY 1997, we show that this law change had a large negative impact
on the college attendance of students with drug convictions. On average, the temporary ban on Federal
financial aid increased the amount of time between high school graduation and college enrollment by
about two years, and we also present suggestive evidence that affected students were less likely to ever
enroll in college. Importantly, we find that the law did not deter young people from committing drug
felonies nor did it substantively change the probability that high school students with drug convictions
graduated from high school. In contrast to much of the existing research, we conclude that, for this highrisk group of students, eligibility for Federal financial aid strongly impacts college investment decisions.

KEYWORDS: Financial Aid, College Enrollment, Drug Felonies
JEL CLASSIFICATION: H30, I28, K14

1

Cornell University, Department of Policy Analysis and Management, Ithaca, NY;14853 mfl55@cornell.edu
Cornell University, Department of Policy Analysis and Management, Ithaca, NY;14853 emily.owens@cornell.edu.
We would like to thank Kirabo Jackson for helpful comments and Blythe McCoy for excellent research assistance.
All errors are our own.
2

1.

Introduction
Changes in the United States economy over the past several decades have led to historically

high returns to obtaining a college degree (e.g., Autor, Katz and Kearney 2008). At the same
time, because the cost of obtaining a college degree is high and growing, liquidity constrained
students may under-invest in higher education. This concern is particularly salient for fragile
populations, such as low-income families and students whose parents do not have a college
education. In order to support lower-income students’ ability to afford college, the Federal
government provides financial assistance to these students, typically in the form of Pell Grants
and Stafford Loans. Federal aid is quite generous – in the 2009-2010 school year alone, the U.S.
government gave out over $42 billion in grant aid and over $100 billion in loan aid to college
students (College Board 2011). A question of central concern is how this aid impacts the
likelihood that high school graduates, in particular those with disadvantaged backgrounds, enroll
in and graduate from college.
Although identifying how financial aid affects college investment decisions is important, due
to the high cost of college and the large amount of money spent on student aid, obtaining
credible estimates of the impact of Federal financial aid on college-going has proved difficult.
Early surveys of college students suggested a positive relationship between student aid and
college enrollment (Leslie and Brinkman 1988). However, quasi-experimental research on the
introduction of the Pell Grant system in 1973 finds little effect of Federal financial aid on college
enrollment (Hansen, 1983; Kane 1994). 1 Faced with these disparate results, education

1

A noted exception to this characterization of the literature is Seftor and Turner (2002), who show that the
introduction of the Pell Grant had a sizable impact on college enrollment among “non-traditional” students, who
begin college in their early 20s and 30s.

1

researchers reviewing the literature typically conclude that the topic “deserves further study”
(Heller 1997).
The lack of strong evidence that Federal financial aid affects college enrollment is in some
ways surprising. Studies that examine state merit aid, or other student aid that does not operate
through the typical Federal formula, tend to find large impacts of financial aid. Dynarski (2003)
examined the 1982 revocation of SSI benefits for college-age children with deceased parents.
Using a difference-in-difference methodology, she finds that each $1000 in SSI aid increased
college enrollment by 3.6 percentage points. Dynarski (2000) studies the introduction of the
Georgia HOPE scholarship, which was introduced in 1993 and provides free in-state tuition to all
Georgia high school graduates with above a 3.0 grade point average. She shows that the
introduction of this program led to an increase in college attendance of between 7 and 8
percentage points. Scott-Clayton (2011) examines a similar program in West Virginia. Using
discontinuities around the GPA cutoff, she estimates that the provision of free tuition
significantly increases postsecondary attainment. Dynarski (2008) also shows evidence that state
merit aid programs increase collegiate attainment.
Of the many plausible explanations for why the Pell and Stafford programs seem to be less
effective than other source of aid, two have gained significant attention. The first explanation is
institutional. In order to receive a Pell grant or Stafford loan, students must fill out the Free
Application for Federal Student Aid, or FAFSA. The 2010-2011 FAFSA consists of over 130
questions about assets and income, similar to the IRS 1040 form. Experimental studies have
found that the effort required to fill out the FAFSA constitutes a substantial barrier to college

2

enrollment (Bettinger et al. 2009). 2 Perversely, this barrier seems to disproportionately affect the
most disadvantaged students, who are the primary targets of the programs (Dynarski and ScottClayton 2007).
The second explanation is methodological. By construction, cross-sectional variation in
Federal student aid is correlated with differences across students in family finances. The amount
of aid available to any particular student is therefore almost certainly correlated with unobserved
factors that also affect the likelihood of investing in college. The 1973 introduction of the Pell
Grant creates a compelling source of variation in aid eligibility, but it is not obvious that the
estimates from the 1970s can be generalized to the current higher education environment. 3 A
lack of exogenous variation across students in aid eligibility makes it difficult to credibly identify
the effect of Federal student aid for college using the current Federal financial aid system.
This paper contributes to the financial aid literature by identifying the impact of a quasiexperimental change in financial aid eligibility for a particular group of disadvantaged students.
The 1998 amendments to the Higher Education Act (HEA98) specified that, beginning in 2001,
any student convicted of a drug offense was ineligible for Federal financial aid for one to two
years post-conviction, depending on whether it was one’s first conviction. We use this change in
a difference-in-difference framework, comparing college attendance among those with and
without drug convictions in the years surrounding the law change, using the 1997 National
Longitudinal Survey of Youth. While not without limitations, this data set allows us to observe

2

The private company Student Financial Aid Services.com charges $80 to $300 for FAFSA assistance. See
http://www.fafsa.com/fafsa-services/pricing-packages.
3
The College Board estimates that, in 2011 dollars, average college tuition in a 4-year public institution was $2,242
in 1981 and $10,144 at a private institution. In 2011, tuition and fees at these institutions had increased to $8,244
and $28,500, respectively (see http://trends.collegeboard.org/college_pricing/report_findings/indicator/884#f8006).
Since the 1990s, the maximum Pell grant has been roughly equal to its original 1973 value relative to average tuition
costs, but the number of people receiving Pell grants has increased over six fold since 1976
(http://www.finaid.org/educators/pellgrant.phtml).

3

detailed criminal history information as well as data on student characteristics, cognitive ability,
and postsecondary investment. The rich individual level data, along with our quasi-experimental
identification strategy, allow us to produce some of the first credible evidence of the causal
impact of Federal financial aid, as it currently is experienced by high school students, on
investment in college.
While the population affected by HEA98 is a select sample of disadvantaged students, this
group is of particular policy interest. Since the law was passed, the fraction of adults with a
criminal history has grown by over 20% (Guerino et al. 2010). At the same time, Federal and
state policy has continued to evolve in a way that has deliberately excluded ex-felons from many
sources of employment and social support, including federal contract work, federally funded
housing assistance, TANF, and food stamps (GAO 2005). To the extent that these policies make
it more difficult for those with criminal records to participate in the legitimate sector, they may
increase the likelihood that these people return to illegal activity. The high social cost of crime
makes any policy affecting outcomes for this high-risk group of individuals worth examining
(Bushway and Sweeten 2007). In addition, it is not clear ex ante that the response of students
with drug convictions to financial aid will differ systematically from the response of
disadvantaged students more generally.
In contrast to the early research on Federal aid, we find that HEA98 significantly and
substantially reduced the probability that students with drug convictions attended college
immediately after graduating from high school. Further tests suggest this is directly related to the
law change. Specifically, we estimate that students with drug convictions took an average of 28
additional months to enroll in college post-HEA98, which is statistically indistinguishable from
the two year ineligibility period specified in the law.
4

The data indicate that students did not delay high school graduation in response to the
eligibility change, and there is no evidence that the HEA98 deterred students from committing
drug crimes. We also conduct a series of permutation tests to verify that our estimated effects are
not driven by outliers. Our estimates are consistent with a small effect of the eligibility change
on the probability students with drug convictions ever attend college or obtain a bachelor’s
degree (BA). However, these estimates are imprecise due to the small number of individuals with
drug convictions who actually attend college. Overall, the largest impact of the law is on delayed
entry into college: HEA98 created an involuntary “double gap year” for the most at-risk students
of an at-risk group. Such delays reduce the returns to a college education, as the higher wages
that accompany collegiate attainment are realized for fewer years.
The paper proceeds as follows: in the next section, we provide additional background on the
HEA98 as well as long run trends in drug convictions. We then describe our data and analytic
approach in section three. Section four presents results, and we conclude with a discussion in
Section five.
2.

The Higher Education Act of 1998 and Juvenile Drug Convictions
The main purpose of the HEA98 was to re-authorize the Higher Education Act of 1965,

which was the original act that set up the current Federal financial aid system. In an apparent
effort to dissuade high school students from engaging in drug-related activities, the HEA98
included a provision that restricts the Federal financial aid eligibility of students who have been
convicted of drug-related offenses. The law states that:
“A student who has been convicted of any offense under any Federal or State law involving the
possession or sale of a controlled substance shall not be eligible to receive any grant, loan, or
work assistance under this title during the period beginning on the date of such conviction…”

5

The ineligibility period is one year for the first conviction, two years for the second, and an
indefinite ban for a third offense. Students can regain eligibility earlier if they complete a drug
rehabilitation program that includes unannounced drug tests. While passed in 1998, the provision
was not enforced until 2001. Between 2001 and 2007, students were asked whether they have
been convicted of possession or sale of illegal drugs in state or federal court. Failure to answer
the drug conviction question makes one ineligible for financial aid (GAO 2005). 4
The eligibility provision in the law does not distinguish between sale and possession
convictions, nor does it distinguish between felony and misdemeanor convictions or State versus
Federal convictions. Any drug offense makes one ineligible. It is important to note, however, that
the Federal government in general, and in particular the Department of Education, lacks the
ability to validate one’s response to this question. Especially for a state-level drug conviction, it
would be very difficult for the government to check whether each student does not have a drug
conviction. 5 While it is illegal to lie on the FAFSA, some students may do so in order to obtain
aid. Using the 2003-2004 National Postsecondary Student Aid Survey (NPSAS), the GAO
(2005) reports that about 41,000 students were denied aid due to a drug-related conviction, which
excludes those who do not apply because of the drug conviction. While a small proportion of the
population, this provision impacts a non-trivial number of students, who as we show below, are
drawn disproportionately from lower socioeconomic backgrounds.
Based on a sample of felony defendants convicted in state courts in 2000, roughly 35% of all
felony convictions were for drug offenses. Roughly 53% of drug offenders were black, and 83%

4

From 2007 onward, students were only asked about convictions that occurred while they were receiving federal
financial aid, meaning that all first-time applicants were eligible on this margin. Our period of analysis extends
through 2003.
5
Bushway et al. (2007) highlight the prevalence of both false negatives and false positives in most criminal
background checks.

6

were male. For sake of comparison, 44% of violent offenders and 39% of property offenders in
that year were black, and 91% and 75%, respectively, were male. The black and male students
most likely to be affected by HEA98 are also the least likely to attend college, ceteris paribus. 6
Also important for our analysis is the fact that drug offenders are more likely than other felons to
have pre-existing criminal records; 44% of those convicted of drug offenses had previously been
convicted of a felony, compared to 39% of property offenders and 33% of violent offenders. 7
Ex Ante, the net social cost of HEA98 is unclear for a number of reasons. First, it is
unclear what, if any effect, this regulation has on college investment. While any increase in the
cost of enrolling in college should reduce the probability that students go, existing research has
failed to find large impacts of Federal aid on college attendance. Furthermore, even if the
marginal impact of Federal aid on attendance was non-zero, the average treatment effect of
HEA1998 may be particularly small, as those with drug convictions may be unlikely to attend
college regardless of financial aid eligibility. 8
Second, even if HEA98 did impact college enrollment, there may be both social costs and
social benefits to this law. If HEA98 discouraged high-risk students from enrolling in college,
any standard model of human capital formation and crime would predict that this would increase
criminal behavior of affected students (Becker 1968, Lochner and Moretti 2003, Mocan et al.
2005). At the same time, to the extent that HEA98 increased the cost of engaging in drug related

6

See Kane (1994) for trends in black-white differences in college enrollment and Bound, Lovenheim and Turner
(2010) and Goldin, Katz, and Kuziemko (2006) for trends in male-female college enrollment. These papers show
that women are more likely to attend college than men and that African American students are less likely to attend
than are white students.
7
See http://www.albany.edu/sourcebook/pdf/t553.pdf.
8
People convicted of drug felonies are generally less civically engaged for reasons besides the conviction (Sweeten
et al. 2009, Hjalmarsson and Lopez 2010).

7

activity, forward looking students may have been deterred by this law. From this deterrence
standpoint, the law could have positive benefits to society as well.
The zero-tolerance approach of HEA98 was consistent with trends in federal drug policy at
the time and was counter to state level movements lowering the expected cost of drug use. In
2000, Nevada, Colorado, and Hawaii became the seventh, eighth, and ninth states to
decriminalize the possession of small amounts of marijuana for personal medical use, 9 which the
U.S. Supreme Court ruled in 2001 was still an unlawful act (USA v. Oakland Cannabis Buyers'
Cooperative (OCBC) and Jeffrey Jones). Neither the state laws nor the Supreme Court ruling
had a clear impact on the likelihood that student with drug convictions attended college. These
states also represent a very small fraction of our sample, and we demonstrate below that the
likelihood of a drug conviction does not shift in 2001, which suggests that these state changes are
unlikely to produce a bias in our estimates. The remainder of this paper examines empirically
how HEA98 affected college investment and drug convictions in order to provide evidence on
the empirical relevance of these costs and benefits of HEA98.
3. Estimating the Impact of HEA98 on College Attendance
3.1. Data
We estimate the impact of HEA98 on the college attendance of drug convicts using the
NLSY97. This nationally representative sample of 12-24 year olds in 1997 contains self reported
data on educational attainment, interaction with the criminal justice system, and a rich set of
demographic characteristics. As in all nationally representative surveys, roughly 1% of
respondents report being convicted of a drug offense, but the fact that we observe both

9

See http://www.npr.org/2011/07/12/126137481/medical-marijuana-laws-a-state-by-state-comparison for a
summary of state marijuana laws.

8

educational and criminal justice outcomes makes it uniquely suited to evaluate the HEA98. 10
However, we do make some minor adjustments to the data set to address issues of plausible
effect size and endogenous selection into the “treatment.”
Any impact of HEA98 on college enrollment may be statistically muted by the inclusion of
NLSY97 respondents who, by construction, either will always or never attend college. We
therefore trim the original NLSY97 sample to include only those respondents who were 12-18 in
1997, because those over the age of 18 likely already have made a decision about college entry.
We also restrict the sample to high school graduates, because these are the students who are on
the margin of college enrollment. While this restriction could bias our estimates if students with
drug convictions are more or less likely to graduate from high school after HEA98, we show
below that no such response is evident in the data.
Our identification strategy consists of comparing the change in college enrollment
likelihoods of students convicted of drug offenses to those who were not before and after 2001.
Determining treatment status thus is critical to accurately identifying any effects of this rule
change on college attendance. Because of the three year delay in when HEA98 went into effect,
students may have anticipated the 2001 change and altered their schooling investment decisions
as a result. We therefore assign each student to a “synthetic cohort” based on the year and month
of birth and then assign students to treatment status based on the year in which they turn 18.

10

For example, in the 2003 Monitoring the Future, roughly 8% of high school seniors reported ever being arrested
(http://www.albany.edu/sourcebook/pdf/t343.pdf). According to the Uniform Crime Reports, overall drug offense
arrest rates were about 0.4% in this time period (http://bjs.ojp.usdoj.gov/content/pub/pdf/aus8009.pdf).

9

Students who turn 18 in the 2000-2001 school year or after are considered to be subject to the
HEA98 provisions. 11
Using the information of the type and dates of convictions we identify, for each student,
whether or not he was convicted of a drug offense in the two years prior to the date of expected
graduation, which is based on his synthetic cohort. For example, if a student is in the synthetic
cohort expected to graduate in spring 2002, he is “treated” if he was convicted of a drug offense
in any time between 2000 and 2002. About 1.2% of the high school graduates in NLSY97 have a
drug conviction within two years of their predicted graduation date. Overall, there are 41 high
school graduates with a drug conviction pre-2001 and 46 in the post-2001 period.
As discussed in Section 2, HEA98 prohibits drug offenders from obtaining financial aid for
different time periods, depending on how many convictions they have. Given the small sample of
students with drug convictions, we use the most expansive definition in order to maximize
power. We therefore use a two-year window, which corresponds to one’s second offense,
because it catches the most students who are potentially affected by the restriction. To the extent
that we mis-classify first offenders with convictions more than a year prior to their FAFSA
application, our estimates will be biased towards zero.
The NLSY97 also contains a large amount of information about student academic and
socioeconomic background that allows us to both test for and control for differential selection
into drug convictions surrounding HEA98. In particular, all respondents are given the Armed
Services Vocational Aptitude Battery (ASVAB), which is a cognitive skills test used by the
military. It is widely used in empirical work to measure student cognitive ability (e.g., Belley and

11

We also have assigned treatment status based on the expected year of graduation using one’s grade in 1997,
assuming each student does not skip or repeat a grade from the time of first observation. This method of assigning
treatment status yields similar results, and these estimates are available upon request from the authors.

10

Lochner, 2007; Lovenheim and Reynolds, 2011a, Lovenheim and Reynolds, 2011b). We also
construct measures of household composition in 1997 (single parent, two parents or other
parental structure), the number of household members under 18, mother’s age at 1st birth,
mother’s age at respondent’s birth, Census region, urban status and household income in 1997.
We control separately for mother’s and father’s educational attainment (less than high school,
high school diploma, some college, college graduate) as well as for gender and race. Table 1
presents descriptive statistics for all controls used in the analysis, which we show separately by
pre- and post-2001 as well as by drug conviction status.
3.2. Estimation Strategy
The estimation strategy we employ is to compare the change in the likelihood of college
enrollment between drug offenders and non-offenders when HEA98 goes into effect in 2001.
The central difference-in-difference model we estimate is as follows:
P ( Atttend ) it = α + δ 1 Post t + δ 2 Convict i + β ( Post t * Convict i ) + ϑX it + λ ( Post t * X it )
+ γ (Convict i * X it ) + ε it

(1)

where Attend is an indicator equal to 1 if the student attends college within two years of high
school graduation. 12 We examine enrollment within two years because of our use of a two-year
window for convictions and in order to focus on “traditional” students who attend college
directly after high school. The variable Post is an indicator for the 2001-2003 synthetic cohorts,
Convict is an indicator for whether the student was convicted of a drug offense in the previous
two years, and X is a vector of observable characteristics that were described in Section 3.1.
Recent work by Bound, Lovenheim and Turner (2010) and Bailey and Dynarsky (2011)
demonstrate a changing relationship between gender, race, family income and college attendance

12

College enrollment includes any enrollment in a two- of four-year school, whether public, private or non-profit.

11

over time. It also is plausible that the impact of having a drug conviction varies by
socioeconomic status; being convicted of a drug offense may matter less for high performing
students, or for those from high income families. We therefore interact all of our control
variables in X it with Post t , and with Convict i , allowing for a more flexible relationship between
demographics and college attendance that may be correlated with treatment status. These
interactions control for any secular shifts in the observable characteristics of student post-HEA98
and control for differences in the relationship between observable characteristics and college
enrollment by drug conviction status.
The coefficient of interest in this model is β, which is the difference-in-difference estimate
conditional on the observable characteristics as well as on those characteristics interacted with
Post and Convict indicators. The central identifying assumption required to interpret β as causal
is that the only reason for a change in the relative enrollment rates between drug offenders and
non-offenders post-2001 is due to the financial aid restrictions in HEA98. The threats to
identification come from the fact that HEA98 did not go into effect for three years after its
passage and only applied to people convicted of drug felonies after 1999 (who would be filling
out the FAFSA in 2001). This lag between the enactment and implementation could cause a
potentially endogenous reduction in the fraction of students committing drug crimes and/or a
strategic manipulation of when someone with a drug arrest was convicted.
We will address this selection problem in several different ways. First, any change in the
types of students who are convicted of drug offenses when HEA98 goes into effect should
become apparent in the extensive set of observable characteristics we observe. For example, if
relatively higher-achieving students were less likely to have drug convictions post-2001, then we

12

might estimate β to be negative, but this positive effect could be due to the fact that convicts
post-2001 were less qualified for college and would not be due to less access to financial aid.
Table 1 presents descriptive statistics of the students in our sample by predicted graduation
date and offender status. The final column of the table provides difference-in-difference
estimates that test whether observable differences between drug offenders and non-offenders
shifted post-2001. First, note that relative to their peers, students with drug convictions are
disadvantaged on almost all margins – their parents have less education, their family incomes are
lower, they are more likely to live in single-parent households, and they are more likely to live in
urban areas. Those convicted of drug offenses also are much more likely to be male. However, as
the D-D estimates show, we cannot reject the null hypothesis that there was no change in this
difference surrounding the implementation of HEA98 in 2001. The difference-in-difference
estimates typically are small relative to the underlying means, and in only one case is this
estimate statistically significantly different from zero at the 5% level. Furthermore, the point
estimates suggest drug offenders are becoming more advantaged over time rather than less
relative to their non-offender counterparts. Drug offenders also are slightly more likely to be
white over time. These differences will serve to bias our estimate of β towards zero in models in
which these observable characteristics are not controlled for. To the extent that there are
unobserved changes in the likelihood of enrolling for college that are correlated with these small
demographic differences, it suggests our difference-in-difference model may understate the
importance of financial aid for college enrollment.
<table 1 about here>
A common criticism of the NLSY97 is that item non-response for key demographic variables
is prevalent. If the pattern of missing data is systematically related to our treatment variables,
13

such non-response is problematic. In Table 2, we present group-level means and difference-indifference estimates of the probability that missing parental education, income, ASVAB score,
and mother’s fertility history are related to the effective date of HEA98. As in Table 1, we find
no evidence of a differential change in the probability that drug offenders and non-offenders do
not report this information, and the estimated magnitude of the differences are small relative to
the group means. 13
<table 2 about here>
Another way to test for selection is to see whether there were differential pre-treatment trends
in college enrollment between drug offenders and non-offenders. In particular, if college
enrollment among drug offenders was declining over time, we could confound this secular
decrease with the effect of the change in the financial aid rule. In Figure 1, we plot the fraction of
people attending college within two years after they graduate from high school, again based on
their predicted year of graduation. Students without drug convictions should not be affected by
HEA98, and indeed there is no shift in college attendance among this group in 2001. Prior to
2001, there is a modest upward trend in the fraction of people with drug convictions that go to
college. But after 2001, the first year that drug offenders were ineligible for federal aid, this trend
reverses. Based on the graphical evidence, there is a roughly 12 percentage point (or 33%) drop
in college attendance, with no recovery by 2003. Furthermore, the same drop is not present for
those charged with a drug offense, as Figure 1 also demonstrates. In fact, college attendance rises
slightly throughout our sample for drug offenders, while it declines precipitously among those
convicted of drug offenses beginning in the 2001 cohort.

13

Note that we include missing indicators in equation (1) interacted with conviction status and the Post dummy.
While it is potentially problematic to include missing data indicators, the fact that data are missing at random with
respect to treatment status suggests there should be little bias from handling missing data in this manner.

14

<figure 1 about here>
Together, Table 1 and Figure 1 show that any bias in our estimate of β must be due to a shift
in the underlying likelihood of attending college among those convicted of drug offenses in the
2001-2003 cohorts relative to the previous cohorts in a manner that is (1) unrelated to the
extensive characteristics we observe and (2) not forecasted by pre-treatment trends. One possible
shift could be an endogenous change in the likelihood of engaging in drug-related behaviors due
to the law. Indeed, the main argument for the drug provisions in HEA98 was to deter teens from
such activities; by raising the cost of conviction, HEA98 may have deterred some individuals
from engaging in drug crimes.
The marginal drug offender deterred by the changes in federal law, including HEA98, would
arguably be more likely to attend college than someone who would engage in drug sales no
matter what, and therefore such a deterrent effect could lead to a spurious negative correlation
between HEA98 and college attendance. The same would be true if police officers, prosecutors,
or judges were less likely to convict marginal drug offenders if it would impact their ability to
receive Federal financial aid.
We can explicitly test for such a deterrent effect by estimating a slight modification of
equation (1), where we analyze whether or not the effective date of HEA1998 changed the
probability that an individual has a drug conviction or was charged with a drug offense. We limit
this analysis to high school graduates, as these are the individuals included in our estimation of
equation (1).
<Table 3 about here>
The results from this analysis are presented in Table 3. When we do not condition on
observables, we actually find that high school graduates are almost 50% more likely to be
15

convicted of a drug felony after HEA98 (column i) and are 30% more likely to be charged with a
drug offense (column iii). This is exactly the opposite effect we would expect in any standard
model of deterrence or compensating behavior on the part of prosecutors. 14 When we condition
on demographic characteristics (columns ii and iv), the direction of the selection effect reverses,
but the magnitude of the selection is less than 1/10 the sample mean and is not statistically
different from zero at conventional levels. We therefore conclude that any contamination of our
treatment effect due to endogenous compositional change is minimal at most. Table 3 also
suggests that the law did not have the intended effect: drug crimes among prospective college
students were not reduced.
Thus, there is little evidence of a demographic shift in the characteristics of drug offenders
surrounding HEA98. Visually, there is a sharp dropoff in college attendance among offenders
when the financial aid provisions of HEA98 come into effect that is not forecasted by pretreatment trends. And, there is no evidence of an endogenous reduction in the likelihood of
getting charged or convicted of a drug crime due to the law. These findings give us confidence
that our estimate of β is identifying the causal estimate of the financial aid restrictions embedded
in HEA98.
4.

Results
Table 4 presents our central difference-in-difference estimates of the effect of HEA98 on

college enrollment. In column (i), we do not condition our estimates on demographic changes,
essentially replicating estimate in the first row of Table 1, and we find a statistically imprecise 12
percentage point reduction in the probability that drug offenders enrolled in college after 2001.
While not precise, this is a large change relative to the pre-2001 attendance rate among drug
14

However, it is consistent with Pfaff (2011), who argues that a large fraction of the increased prison population is
due to prosecutors filing more felony charges, conditional on arrest.

16

offenders (36%), and it also is large relative to the 27 percentage point difference in the college
attendance rate across convicts and their peers (see Table 1). While suggestive of a large impact
of financial aid on two-year enrollment, the small number of convicts renders this estimate rather
imprecise.
We next add in controls for observable characteristics and their interactions with the
treatment indicators sequentially. In column (ii), we include our basic controls for demographic
characteristics. Variation in the composition of high school graduates explains much of the trend
in attendance rates over time and slightly mitigates the differences in college attendance for
offenders and non offenders. Conditional on demographics, we estimate that excluding drug
offenders from aid eligibility reduces the probability they enrolled in college within two years of
graduating high school by 16 percentage points, which is statistically different from zero at the
10% level. This is a 44% decline relative to the baseline of 36%.
<Table 4 about here>
Finally, in column (iii), we show our preferred specification, in which we relax our
constraints on the relationship between individual characteristics and college enrollment over
time and across groups. In contrast to the existing literature that finds negligible effects of
FAFSA-based Federal aid on college enrollment, we estimate that when drug felons were
excluded from Federal aid, there was a 22 percentage point (or 61%) reduction in the probability
that they attended college immediately after high school. We can reject the null hypothesis that
this effect is different from zero at the 5% level, but given our small sample sizes the standard
error bounds still encompass small and very large effects. Given the lack of findings in previous
work that Federal financial aid affects college-going, this estimate is almost incredibly large.
Based on college attendance in the NLSY97, denying drug offenders Pell grants and Stafford
17

loans may have been functionally equivalent to preventing them from attending college for at
least two years after graduating from high school.
Because our college attendance estimate examines two-year enrollment, it may confound
the effects of HEA98 on delayed attendance and on ever attending college. In Table 5, we exploit
the richness of the education data in the NLYS97 to better understand how HEA98 affected drug
offenders. We include the full set of demographic controls and their interactions with Conviction i
and Post t in all reported specifications.
<Table 5 about here>
In column (i), we show that, while HEA98 prevented drug offenders from attending college
immediately after high school, there is weaker evidence that a temporary restriction on Federal
aid permanently reduced the chances that someone attended college. 15 Drug offenders were 8
percentage points less likely to ever attend college, but this point estimate is smaller than the
standard error and about 1/5 of the underlying mean likelihood of ever attending college. This
estimate is suggestive of a long-run effect, but given the wide confidence interval this result is
not definitive. Consistent with a small long-run effect, we also find only suggestive evidence that
HEA98 reduces the probability that high school students with drug offenses graduate from a
four- year college (column ii). While our estimate is large relative to the baseline graduation rate
pre-2001 among drug offenders, the fact that very few students who have drug convictions
obtain a BA regardless of financial aid eligibility implies that we have a limited ability to detect
any effect on college completion given our small sample size of drug offenders.

15

The most recent year of NLSY97 data is 2009. So, by “ever attend college” we refer to the likelihood our
respondents attend by 2009. In 2009, the youngest cohort is 25, and while college attendance among older students
is rising, the vast majority of college students first attend college by their early 20s (Fitzpatrick and Turner 2007).

18

The HEA98 stipulated that after one to two years drug offenders would once again be
eligible for Federal aid, depending on the number of past offenses. The temporary nature of the
ban makes time to enrollment a natural outcome of interest. In column (iii), we estimate that, on
average, after 2001, drug offenders delayed college enrollment by 28 months (se=8.01). 16 There
is an 80% chance that drug offenders waited exactly 24 months, the amount of time HEA98
required them to wait before becoming eligible for aid, to enroll in college. Thus, it appears that
the main effect of the law was to delay college entry, which creates potentially significant costs
for students who have to wait several years longer to obtain the returns to a college education. 17
Drug offenders may have strategically manipulated when they graduated from high school in
anticipation of being temporarily ineligible for Federal aid. In column (iv) of Table 5, we
estimate the amount of time it took each individual to complete high school and find some
evidence consistent with strategic behavior. On average, students with drug offenses who are
predicted to graduate after 2001 took almost 4 more months to complete high school. This effect
is relatively small but is imprecisely estimated. At the same time, in column (v) we show that
HEA98 did not reduce the long-run likelihood of ever graduating from high school. This is an
important result, as it suggests that our decision to condition on high school graduation should
not introduce a large bias to our estimates. Furthermore, these results imply that the vast majority
of the increased delay in time to college enrollment among offenders in the 2001-2003 cohorts is
due to waiting to enroll in college post-high school, rather than due to later high school
graduation.

16

Note that time between high school and college enrollment is measured as of the actual month of high school
graduation, not of the predicted month of graduation based on one’s synthetic cohort.
17
While most of these students will not obtain a BA, there is ample evidence in the literature of sizable returns to
sub-baccalaureate training (e.g., Kane and Rouse 1995; Andrews, Li and Lovenheim 2011; Jepsen, Troske and
Coomes 2011).

19

< Figure 2 about here >
One potential limitation of our analysis is that, because of the small number of “treated”
individuals, our estimates may be driven by a few outliers. In order to address this issue, we
conducted a series of permutation tests. First, we re-estimated our preferred model, Table 4
column (iii), 46 times, excluding one treated individual each time. Panel A of Figure 2 presents
all of estimates treatment effects from these regressions along with the bounds of the 95%
confidence interval. All estimates are statistically different from zero at the 5% level and range
from -0.24 to -0.18. We then systematically eliminate each possible pair of treated individuals
from our sample. These 1,036 different regressions, presented in Panel B of Figure 2, produce
average treatment effects ranging from -0.27 to -0.15, and 97.4% of them are statistically
different from zero. Based on these tests, we conclude that, even with our limited sample, our
results are unlikely to be statistical anomalies.
<Table 6 about here >
Finally, in order to verify that we are picking up the impact of the HEA98 financial aid
restrictions rather than some unobserved shift in the composition of drug offenders or some
contemporaneous unobserved shock, we conduct a series of falsification tests in which we vary
our definition of “drug offenders.” Again, the richness of the NLYS97 allows us to differentiate
people who interacted with the criminal justice system but did not in the specific way that would
make them ineligible for Federal loans and grants.
First, in columns (i) and (ii) of Table 6, we replace Convicted i with Charged i . Since our
treated group now includes individuals who were arrested and charged with drug crimes in
addition to those who ended up being convicted, we expect that our treatment effect will be
attenuated. Indeed, this is what we find. Columns (i) and (ii) of Table 6 show that the impact of
20

delayed eligibility falls by 75% under this definition, and it no longer is statistically significant at
even the 10% level. In columns (iii) and (iv), we verify that the difference between column (ii)
of Table 6 and column (iii) of Table 4 is driven by these unaffected drug users by restricting our
treated group to those who are charged, but not convicted, of drug offenses. We estimate the
HEA98 caused an imprecise 6 percentage point increase in the probability that these students
attended college the year after high school when we control for observables. Thus, the effects we
estimate in our baseline models are not driven by differential impacts of interaction with the
criminal justice system post-HEA98 but are driven by the differential impact of being convicted,
which is consistent with the structure of HEA98.
In columns (v) and (vi) of Table 6, we focus on students who were convicted of drug
offenses at least three years before they were predicted to graduate high school. Consistent with
the language of HEA98, we find no evidence that these students were any less likely to enroll in
college after high school. If anything, students with older drug convictions are more likely to
attend college after 2001, but this estimate is very imprecisely estimated. Overall, Table 6 shows
that the effects we estimate in Tables 4 and 5 are due to the differential effects of having a drug
conviction within two years in the 2001-2003 cohorts, which gives us some confidence our
estimates are identifying the causal impact of HEA98 on college enrollment behavior because
this is the group one would expect to be affected given how the law is written.
Finally, in the last two columns, we perform a final falsification test, exploring the impact of
HEA98 on students convicted of non-drug offenses, such as violent crimes (e.g., assault or
robbery), property offenses (e.g., burglary) and major driving offenses (e.g., drunk driving).
While conviction for any of these offenses could result in incarceration, HEA98 did not affect
the federal financial aid eligibility of these students. We estimate that, after the effective date of
21

HEA98, high school seniors convicted of serious crimes are roughly 7 percentage points less
likely to attend college within two years of graduating high school, which is 1/3 of the change for
drug offenders.
Recall that, in a given year, roughly 40% of adults convicted of a drug offense have been
convicted of some sort of felony in the past. Since criminals, especially juveniles, tend to
commit multiple types of crimes (Blumstein et. al 1988), it is not surprising that about 20% of
students in our sample with a drug conviction also have been convicted of another crime. In the
final column of Table 6, we control for both the presence of a drug conviction and a non-drug
conviction, allowing us to better address this confounding issue. These controls reduce the
magnitude of the statistically imprecise impact of non-drug convictions by almost half, implying
that the larger “treatment effect” estimated in column (vii) was due to non-drug offenders also
having drug convictions. Column (viii) shows little evidence of a shift in the likelihood of a
student with a non-drug offense attending college in 2001, while the estimate for drug offenders
still is large and is statistically significant at the 10% level. Thus, consistent with the provisions
in HEA98, only students with drug convictions reduced college enrollment in 2001, suggesting
this reduction was a response to lack of access to Federal financial aid rather than due to
underlying trends in college participation among those with criminal convictions.
5.

Conclusion
Due to the rising costs of college attendance and the growing importance of collegiate

attainment for life outcomes, understanding how financial aid impacts postsecondary enrollment
is of high importance. It is particularly important identify the role of financial aid for
underprivileged students, who attend college at much lower rates than their wealthier
counterparts. Students who are convicted of felony drug charges are arguably among the most at22

risk students in America. While their performance on achievement tests is comparable to their
peers, these student come from poorer families with non-traditional parental arrangements, and
their parents are less likely to have attended college. Furthermore, being convicted of any felony
offense at a young age is a strong predictor of future violent criminal behavior (Blumstein and
Cohen 1987). The opportunity cost of allowing these young people to continue to fail, while
difficult to quantify, is inarguably large.
Despite the importance of identifying the effect of financial aid in general and Federal
financial aid in particular on college enrollment, the previous literature has not reached a
consensus, due predominantly to the difficulty in generating exogenous variation in aid access.
This paper exploits a rule change from the Higher Education Act of 1998 that temporarily
eliminated Federal financial aid eligibility for students convicted of a drug offense in the
previous two years. We show extensive evidence that this rule change created an exogenous
decrease in financial aid eligibility for students with a drug conviction.
Using NLSY97 data on college enrollment, student socioeconomic and cognitive
backgrounds and criminal histories, we employ a difference-in-difference methodology that
examines how college enrollment among drug offenders relative to non-offenders changed
surrounding the implementation of HEA98 in 2001, the first year this rule went into effect. We
find evidence that the temporary prohibition on Federal aid caused a large decline in the fraction
of drug offenders who enrolled in college within two years of graduating from high school. This
decline was driven predominantly by elongating the time between high school and college; drug
offenders on the margin of college enrollment simply waited to enroll until they were eligible
again for aid. The effects on ever attending college (by 2009) and on BA completion are more
modest. This elongation has costs, however, in the form of delaying the returns to collegiate
23

attainment. In addition, we find no evidence that the law had a deterrent effect on drug offenses.
Thus, by forcing drug offenders to wait two years before enrolling in college, HEA1998 lowered
the lifetime earnings of these at-risk students without generating benefits to society through
reduced crime.
While this paper identifies the effect of Federal financial aid on college enrollment among a
distinct set of students – drug offenders – they are of high interest because they are from low
socioeconomic backgrounds and because they are at-risk of committing more crime in the future.
Attending college may be an important “turning point” in the lives of delinquent youths, on par
with marriage or employment (Sampson and Laub 1990, Uggen 2000); education, in particular
post-secondary education, is strongly correlated with desistance from crime (Nuttall et al. 2003,
Johnson 2001, Clark 1991). By restricting access to financial aid, HEA98 may have
inadvertently harmed the long-run life outcomes of these at-risk students. Indeed, in our sample
students with drug convictions are 0.8 of a percentage point (se=0.5), or 60%, more likely to be
convicted of another drug crime in the three years after high school graduation if they are subject
to the HEA98 financial aid restrictions.
Despite the selected sample, this paper is the first in the literature to show evidence that
modern Federal financial aid impacts college decisions, and there is little reason to believe lowincome students more generally respond in a fundamentally different way to the availability of
this aid. Given the importance of understanding how Federal financial aid impacts college-going
decisions, more research on the impact of this aid on a more general group of students is needed.

24

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27

Table 1: Means and Standard Deviations of Analysis Variables
Variable
Attend College
ASVAB (10,000 units)
Household Income ($10,000)
Single Parent
Two Parents
Other Parental Structure
# HH Members < 18
Urban
Mom Age at 1st Birth
Mom Age at Respondent Birth
Northeast
North Central
South
West
Mother < High School
Mother High School Diploma
Mother Some College
Mother BA+
Father < High School
Father High School Diploma
Father Some College
Father BA+
Black
Hispanic
Male
Observations

Pre-Change
Conviction No Conviction
0.623
0.358
(0.485)
(0.485)
5.390
5.027
(2.798)
(2.543)
5.647
4.419
(4.599)
(2.635)
0.262
0.397
(0.440)
(0.495)
0.687
0.462
(0.464)
(0.505)
0.051
0.141
(0.220)
(0.352)
2.219
2.207
(1.178)
(1.154)
0.686
0.884
(0.464)
(0.325)
23.35
23.86
(4.62)
(4.98)
25.72
25.68
(5.38)
(4.83)
0.188
0.301
(0.391)
(0.464)
0.274
0.170
(0.446)
(0.380)
0.332
0.330
(0.471)
(0.476)
0.205
0.199
(0.404)
(0.404)
0.148
0.094
(0.356)
(0.295)
0.381
0.426
(0.486)
(0.502)
0.253
0.291
(0.435)
(0.460)
0.218
0.190
(0.413)
(0.398)
0.161
0.228
(0.368)
(0.427)
0.367
0.521
(0.482)
(0.509)
0.202
0.170
(0.401)
(0.383)
0.271
0.080
(0.444)
(0.277)
0.193
0.144
(0.400)
(0.351)
0.156
0.121
(0.368)
(0.326)
0.811
0.503
(0.396)
(0.500)
3,958

41

Post-Change
Conviction No Conviction
0.651
0.269
(0.477)
(0.448)
5.435
5.753
(2.773)
(2.475)
5.500
4.137
(4.558)
(2.707)
0.241
0.367
(0.428)
(0.487)
0.719
0.605
(0.450)
(0.494)
0.040
0.028
(0.196)
(0.168)
2.424
2.360
(1.145)
(0.974)
0.690
0.813
(0.463)
(0.394)
23.76
24.17
(4.78)
(4.94)
26.40
27.09
(5.30)
(5.36)
0.183
0.231
(0.387)
(0.426)
0.267
0.229
(0.443)
(0.425)
0.333
0.428
(0.450)
(0.500)
0.217
0.112
(0.412)
(0.319)
0.145
0.174
(0.392)
(0.384)
0.350
0.256
(0.477)
(0.442)
0.268
0.209
(0.443)
(0.412)
0.237
0.361
(0.425)
(0.486)
0.152
0.166
(0.359)
(0.378)
0.385
0.499
(0.487)
(0.508)
0.201
0.197
(0.401)
(0.404)
0.261
0.138
(0.439)
(0.350)
0.130
0.144
(0.340)
(0.351)
0.072
0.117
(0.262)
(0.321)
0.819
0.498
(0.390)
(0.500)
3,356

46

D-D
-0.117
(0.104)
0.681
(0.710)
-0.134
(1.167)
-0.009
(0.094)
0.111
(0.099)
-0.110∗∗
(0.045)
-0.052
(0.250)
-0.074
(0.100)
-0.10
(1.06)
0.73
(1.21)
-0.066
(0.084)
0.066
(0.096)
0.098
(0.101)
-0.098
(0.088)
0.084
(0.080)
-0.139
(0.109)
-0.097
(0.099)
0.153
(0.095)
-0.053
(0.093)
-0.041
(0.124)
0.027
(0.103)
0.067
(0.113)
-0.064
(0.076)
-0.080
(0.070)
0.013
(0.107)
7,401

All tabulations include only high school graduates. Standard deviations are in parentheses in the first four
columns and standard errors are in parentheses in the D-D column: ** indicates statistical significance at
the 5% level and * indicates statistical significance at the 10% level.

28

Table 2: Means and Standard Deviations of Missing Indicator Variables
Variable
Mother’s Education Missing
Father’s Education Missing
Family Income Missing
ASVAB Missing
Mom Age at 1st Birth Missing
Mom Age at Respondent Birth Missing

Pre-Change
Conviction No Conviction
0.066
0.100
(0.249)
(0.303)
0.156
0.283
(0.363)
(0.456)
0.260
0.250
(0.438)
(0.438)
0.172
0.293
(0.378)
(0.461)
0.068
0.099
(0.252)
(0.303)
0.058
0.099
(0.233)
(0.303)

Post-Change
Conviction No Conviction
0.058
0.073
(0.233)
(0.263)
0.142
0.245
(0.349)
(0.435)
0.222
0.306
(0.416)
(0.466)
0.163
0.252
(0.369)
(0.439)
0.067
0.069
(0.251)
(0.256)
0.054
0.069
(0.227)
(0.256)

D-D
-0.018
(0.052)
-0.025
(0.077)
0.094
(0.092)
-0.032
(0.081)
-0.030
(0.054)
-0.027
(0.050)

All tabulations include only high school graduates. Standard deviations are in parentheses in the first four columns
and standard errors are in parentheses in the D-D column: ** indicates statistical significance at the 5% level and
* indicates statistical significance at the 10% level.

Table 3: Effect of The Financial Aid Policy
Change on Drug Charges and Convictions
Independent Variable
Post-Change
Observables
Dep. Var. Mean

I(Convicted)
(i)
(ii)
0.005∗ -0.001
(0.003) (0.007)
No

Yes
0.012

I(Charged)
(iii)
(iv)
0.007∗ -0.001
(0.004) (0.010)
No

Yes
0.023

All estimates include only high school graduates. Standard
errors are in parentheses: ** indicates significance at the 5%
level and * indicates significance at the 10% level.

29

Table 4: Effect of Conviction on College
Enrollment Surrounding Eligibility Policy Change
Independent Variable

(i)
-0.266∗∗
(0.083)
0.028∗∗
(0.012)
-0.117
(0.108)

(ii)
-0.180∗∗
(0.069)
0.005
(0.022)
-0.160∗
(0.091)

(iii)
0.812∗∗
(0.452)
-0.046
(0.086)
-0.220∗∗
(0.091)

R2

0.006

0.235

0.242

Observables
Observables*Post
Observables*Convicted

No
No
No

Yes
No
No

Yes
Yes
Yes

Convicted
Post-Change
Post*Convicted

All estimates include only high school graduates.
Heteroskedasticity-robust standard errors are in parentheses: ** indicates significance at the 5% level and *
indicates significance at the 10% level.

30

Table 5: Effect of Conviction on College and High School Outcomes
Surrounding Eligibility Policy Change

Independent Variable
Convicted
Post-Change
Post*Convicted
Pre-HEA98
Offender Mean
1

2

Ever Attend
College
(i)
0.928∗
(0.473)
0.006
(0.083)
-0.080
(0.105)

0.410

BA
(ii)
0.909∗∗
(0.317)
-0.002
(0.079)
-0.072
(0.051)

0.074

Time Between
HS & Coll.
(iii)
52.50
(32.06)
5.86∗
(3.40)
27.98∗∗
(8.01)

8.44

Time to
HS Degree
(iv)
16.26
(15.53)
6.98∗∗
(1.78)
3.82
(2.79)

HS
Degree
(v)
-1.068∗∗
(0.319)
-0.109∗
(0.060)
0.075
(0.068)

242.85

0.631

The “Pre-HEA98 Offender Mean” is the mean of the drug convict sample pre-2001. All
estimates except the final column include only high school graduates. The Time to HS
Degree is enumerated by the number of months since January 1, 1980.
Heteroskedasticity-robust standard errors are in parentheses: ** indicates significance at
the 5% level and * indicates significance at the 10% level.

31

Table 6: Falsification Tests

Independent Variable
Convicted/Charged
Post-Change
Post*Convicted/Charged
Non-Drug Conviction
Post*Non-Drug Conviction
Observables
Observables*Post
Observables*Convicted/Charged
1

2

Charged in Last
Two Years
(i)
(ii)
-0.220∗∗
0.368
(0.061)
(0.325)
0.026∗∗ -0.046
(0.012)
(0.086)
0.015
-0.056
(0.083)
(0.076)
.
.
.
.
.
.
.
.
No
No
No

Yes
Yes
Yes

Charged but
Not Convicted
(iii)
(iv)
-0.176∗∗
0.276
(0.085)
(0.432)
0.026∗∗ -0.037
(0.012)
(0.076)
0.172
0.058
(0.117)
(0.102)
.
.
.
.
.
.
.
.
No
No
No

Yes
Yes
Yes

Convicted Three or
More Years Ago
(v)
(vi)
-0.621∗∗ -0.376∗∗
(0.008)
(0.083)
0.025∗∗ -0.046
(0.011)
(0.086)
-0.025
0.137
(0.304)
(0.103)
.
.
.
.
.
.
.
.
No
No
No

Yes
Yes
Yes

Including NonDrug Convictions
(vii)
(viii)
.
-0.091
.
(0.075)
-0.006
-0.012
(0.083) (0.083)
.
-0.166∗
.
(0.100)
0.035
0.007
(0.224) (0.224)
-0.069
-0.036
(0.057) (0.059)
Yes
Yes
Yes

Yes
Yes
Yes

All estimates include only high school graduates. The estimates in columns (iii) and (iv) examine those who were
charged with a drug offense in the past two years but who were not convicted. Estimates in columns (v) and (vi)
examine those who have a drug conviction more than two years prior to the synthetic cohort graduation year. In the
final two columns, we analyze non-drug offenses on the prior two years and drug and non-drug offenses simultaneously.
Heteroskedasticity-robust standard errors are in parentheses: ** indicates significance at the 5% level and * indicates
significance at the 10% level.

32

.6

Figure 1: Trends in College Enrollment Rates by Conviction Status and High
School Cohort
Drug Conviction

.1

College Attendance Rate (Within 2 Years)
.2
.3
.4
.5

No Convictions
Drug Charge

1998

1999

2000
2001
Predicted HS Graduation Year

2002

2003

Source: Author’s calculations from the 1997 National Longitudinal Survey of Youth as described in the
text.

33

Figure 2: Permutation Tests

−.5

−.4

Coefficient Estimate
−.3
−.2
−.1

0

.1

Panel A: Removing 1 Observation

0

.1

.2

.3
.4
.5
.6
.7
Cumulative Percent of Estimates

.8

.9

1

.9

1

−.5

−.4

Coefficient Estimate
−.3
−.2
−.1

0

.1

Panel B: Removing 2 Observations

0

.1

.2

.3
.4
.5
.6
.7
Cumulative Percent of Estimates

.8

Source: Author’s calculations from the 1997 National Longitudinal Survey of Youth as described in the
text. In Panel A, we remove each of the 46 treated observations and re-estimate the model. The figure
shows the inverse CDF of the resulting estimates with the bounds of the 95% confidence interval. In Panel
B, we remove each pair of two treated estimates and plot the inverse CDF of resulting estimates along with
the bounds of the 95% confidence interval.

34