NORC at the University of Chicago
Teen Drinking and Educational Attainment: Evidence from Two‐Sample Instrumental
Variables Estimates
Author(s): Thomas S. Dee and William N. Evans
Source: Journal of Labor Economics, Vol. 21, No. 1 (January 2003), pp. 178-209
Published by: The University of Chicago Press on behalf of the Society of Labor
Economists and the NORC at the University of Chicago
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178
[ Journal of Labor Economics, 2003, vol. 21, no. 1]
᭧ 2003 by The University of Chicago. All rights reserved.
0734-306X/2003/2101-0006$10.00
Teen Drinking and Educational
Attainment: Evidence from TwoSample
Instrumental Variables Estimates
Thomas S. Dee, Swarthmore College and National Bureau
of Economic Research
William N. Evans, University of Maryland, Project Hope,
and National Bureau of Economic Research
This study examines the effects of teen alcohol use and availability on
educational attainment. We demonstrate that teens who faced a lower
minimum legal drinking age (MLDA) were substantially more likely
to drink. However, we find that changes in MLDA had small and
statistically insignificant effects on educational attainment. Using
matched cohorts from two data sets, we also report two-sample instrumental
variables estimates of the effect of teen drinking on educational
attainment. These estimates are smaller than the corresponding
ordinary least squares estimates and statisticallyinsignificant,indicating
that teen drinking does not have an independent effect on educational
attainment.
This manuscript is a revised version of National Bureau of Economic Research
Working Paper no. 6082. We wish to thank Ed Montgomery, Wallace Oates, John
Shea, Judy Hellerstein, and Bob Schwab for a number of helpful comments.
Thomas Dee gratefully acknowledges the support of the American Educational
Research Association (AERA), which receives funds for its AERA Grants Program
from the National Science Foundation (NSF) and the National Center for
Education Statistics (U.S. Department of Education) under NSF Grant RED-
9452861. William Evans gratefully acknowledges the NSF, which supported this
research under NSF Grant SBR-9409499. The opinions expressed here are ours
and do not necessarily reflect those of the granting agencies.
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Teen Drinking and Educational Attainment 179
I. Introduction
The abuse of alcohol is widely recognized as a major social problem
with important health consequences for consumers and those around
them.1
Because the habit of abusing alcohol may be developed early and
have significant implications for life-cycle decisions, much of the research
on alcohol consumption has focused on the behavior of teens.2
One widely
cited conclusion of this literature is that the youthful consumption of
alcohol inhibits the accumulation of schooling (Mullahy and Sindelar
1989; Cook and Moore 1993, 1999; Yamada, Kendix, and Yamada 1996).
Based, in part, on this conclusion, several authors have recommended
policies that reduce alcohol availability through higher taxes (Grossman,
Chaloupka, et al. 1993; Grossman, Sindelar, et al. 1993; Cook and Moore
1994, 1999).3
However, there is reason to question whether these recommendations
have sound empirical support. Some of the prior research,
for example, has assumed that the decision to drink is made independently
of schooling decisions.4
Furthermore, as we demonstrate in this study,
evaluations that have recognized the potential endogeneity of these decisions
may be misspecified since they rely solely on the cross-state variation
in excise taxes on beer and minimum legal drinking ages (MLDA)
as exogenous determinants of teen drinking.
The first section of this article uses the National Education Longitudinal
Study of 1988 (NELS-88) to establish an empirical baseline: teens who
drink are less likely to complete high school and less likely to enter college.
We also present results that promote the suspicion that the drinkingschooling
relationship reflects correlation rather than causation. Specifically,
in a sample of high school seniors who did not drink as sophomores,
eighth- and tenth-grade test scores are lower among those who drank in
twelfth grade, suggesting that students who are low academic achievers
in their early teen years are more likely to drink heavily as seniors.
These results suggest that models of educational attainment that treat
1
Most notably, alcohol use is strongly implicated in the leading cause of mortality
among young adults: traffic fatalities (National Highway Traffic Safety Administration
2000). However, the use and availability of alcohol has been linked
to other outcomes such as liver cirrhosis, smoking participation, teen childbearing,
fetal health, crime, earnings, and marriage (Grossman, Sindelar, et al. 1993; Cook
and Moore 1994; Kenkel and Ribar 1994; Dee 1999a, 2001; National Institute on
Drug Abuse 1999).
2
Teens also have higher rates of alcohol abuse and are involved in a disproportionate
number of traffic accidents (Grant et al. 1991; National Institute on
Alcohol Abuse and Alcoholism 1996).
3
Though all states now have an MLDA of 21, the issue of whether this requirement
should be changed has also been under consideration in several states
(e.g., “Louisiana Stands Alone,” 1996; “Va.’s Cullen Urges Look,” 1997).
4
However, the problems of establishing causality in schooling/health relationships
have been recognized by other researchers (e.g., Kenkel 1991).
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180 Dee/Evans
teen drinking as exogenous may overstate the true effect of teen drinking.
Recognizing this, Cook and Moore (1993) utilized the changes in drinking
generated by the cross-state variation in the MLDA and beer taxes to
identify the causal effects of teen alcohol consumption on educational
attainment.5
They concluded that teen drinking significantly reduces educational
attainment. Their primary evidence consisted of reduced-form
estimates of the effect of beer taxes on school persistence. However, this
identification strategy may be misleading since the instruments represent
not only the availability of alcohol but also the unobserved state attributes
that influence teen drinking and educational attainment (Dee 1999b).
A more convincing identification strategy would condition on unobserved
state attributes and rely on the within-state variation in alcohol
availability over time. To this end, we have used the increases in MLDA
during the 1980s as an exogenous determinant of teen drinking. In 1977,
30 states had an MLDA of 18. By 1989, largely because of federal pressure,
all states had raised their MLDA to 21. Using data on teen drinking from
the 1977–92 Monitoring the Future (MTF) surveys, we demonstrate that
teens who faced an MLDA of 18 were substantially more likely to drink
than teens who faced a higher drinking age.6
However, models that exploit
the within-state variation in beer taxes over time suggest that this policy
instrument has had no detectable effect on teen drinking (Dee 1999b).
If teen drinking did have an independent effect on human capital accumulation,
then educational attainment within states should have risen
after the MLDAs were increased. We test this hypothesis using data on
over 1.3 million respondents who belonged to the 1960–69 birth cohorts
in the Census Bureau’s 1990 5% Public-Use Microdata Sample (PUMS).
We find that teen exposure to an MLDA of 18 had small and statistically
insignificant effects on indicators for high school completion, college entrance,
and college persistence. Using the two-sample instrumental variables
(TSIV) procedure developed by Angrist and Krueger (1992, 1995),
we combine the first-stage and reduced-form results to generate estimates
of the effect of teen drinking on educational attainment. These TSIV
estimates are smaller than the corresponding ordinary least squares (OLS)
estimates and are statistically insignificant, indicating that teen drinking
does not have an independent effect on educational attainment. The final
section discusses the policy implications of these results.
5
In fact, most of the literature addressing the policy determinants of teen drinking
has relied on the cross-state variation in availability (Grossman et al. 1987;
Coate and Grossman 1988; Grossman, Chaloupka, et al. 1993; Grossman, Sindelar,
et al. 1993; Kenkel 1993; Cook and Moore 1994).
6
We also discuss some evidence that supports the maintained assumption that
the variation in MLDA is independent of trends in teen drinking.
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Teen Drinking and Educational Attainment 181
II. An Empirical Baseline
The consumption of alcohol could reduce an individual’s educational
attainment through several mechanisms. Abusing alcohol may inhibit the
ability and opportunity to learn as well as increase exposure to activities
that have severe consequences such as drunk driving (see, e.g., National
Highway Traffic Safety Administration 2000; Dee and Evans 2001), accidents,
violence (see, e.g., Markowitz 2000), sexually transmitted diseases
(see, e.g., Chesson, Harrison, and Kessler 2000), and teen childbearing
(see, e.g., Dee 2001). Furthermore, available options for future schooling
may be curtailed through an effect on current academic performance and
through the development of a habit with negative implications for future
achievement. This section sets a baseline for discussing whether these
effects exist by estimating the probability that teen drinkers complete high
school and go on to college. We also present some suggestive evidence
that these correlations may be subject to an omitted variable bias.
These evaluations are based on the National Center for Education Statistics’
(NCES) NELS-88. This survey began with a nationally representative
sample of eighth graders in 1988. The base-year sample was constructed
in two stages. The first stage produced a sample of 1,052 grade
schools, and in the second stage a random sample of students from within
these schools were selected. Nearly 25,000 students were interviewed in
the base year. Follow-up interviews occurred in 1990, 1992, and 1994.
The “core” sample of respondents for the follow-ups consisted of a stratified,
random sample of base-year respondents. However, the sample was
also “freshened” with new respondents so that nationally representative
cross-sections of tenth graders in 1990 and twelfth graders in 1992 could
be constructed.
We have defined high school completion and college entrance for the
NELS-88 respondents by using responses to the third follow-up survey
that occurred in 1994. In order to make these estimates as consistent as
possible with the restrictions imposed by the other data sets we will use
in later sections, we have included among high school completers those
who have earned equivalency degrees.7
Furthermore, we have, for the
same reason, restricted our samples to include only black, white, and
Hispanic respondents. We have also defined college entrants as those
whose highest postsecondary status in 1994 involved working toward a
bachelor’s degree.
During the first two follow-ups in 1990 and 1992, NELS-88 respon-
7
The 1990 PUMS employs a similar definition of high school completion. There
is some evidence that this construction is inappropriate since equivalency degrees
may be poor substitutes for graduating on time (Cameron and Heckman 1993).
The correlation of drinking with finishing high school on time is somewhat
stronger than that suggested by this construction.
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182 Dee/Evans
dents were asked about the frequency and the quantity of their alcohol
consumption. As in other empirical research on teen drinking, we have
defined a drinker as a teen who reports having had at least one drink in
the last month. A heavy drinker reports having had five or more drinks
in a row at least once in the last 2 weeks. In 1990, 42% of NELS-88 tenth
graders had a drink within the last month, and 23.6% had drunk heavily
within the past 2 weeks. Among NELS-88 twelfth graders in 1992, 52.1%
had a drink within the past month, while about 28.8% had drunk heavily.8
While there is concern that such self-reported consumption may understate
actual use, the levels of drinking reported in the NELS-88 data are
quite consistent with the contemporaneous data from other widely used
surveys.9
Furthermore, validation studies based on longitudinal surveys
like MTF indicate that adult recalls about teen substance use are highly
consistent with the responses as teens, which suggests the reliability of
the self-reported data (e.g. O’Malley, Bachman, and Johnston 1983). There
is also evidence that youths are less likely to underreport substance use
in school-based surveys such as NELS-88 and MTF than in other household-based
surveys (e.g. Gfroerer, Wright, and Kopstein 1997).
Using this information on self-reported teen drinking and subsequent
educational attainment, we generated stylized evidence on the partial correlations
between teen alcohol use and schooling decisions. More specifically,
using the 1990 tenth graders, we report the “effects” of sophomore
drinking on the probability of completing high school and on the probability
of entering college. Using the 1992 twelfth graders, we also report
the “effect” of senior drinking on the probability of entering college.
Table 1 reports the estimated coefficients on the drinking variables in
linear probability models where the outcomes of interest are the discrete
variables high school completion and college entrance.10
The first two
columns report estimates for high school completion models for the sophomore
class, while the next four columns report estimates from college
entrance models for the sophomore and senior classes, respectively. As
we move down the table, we include additional controls for family income,
family structure, and parental education, plus school fixed-effects.11
These
8
These means may not be nationally representative because we do not use
sample weights. Our econometric work also does not use sample weights.
9
For example, in the 1992 MTF data that are presented later, 50.2% of high
school seniors report being drinkers; 26.7% report being heavy drinkers.
10
We report linear probability estimates instead of probit models to hold constant
the estimation procedure when we compare OLS and two-sample instrumental
variable estimates. In the latter models, we estimate linear regression models
in order to construct the instrumental variables estimates. The results of probit
models, however, are quite similar to those reported in table 1.
11
These parent-reported family traits were represented in an unrestrictive manner
by 15 dummy variables for family income, six for family structure, and four
for parental education.
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Table 1
Linear Probability Estimates of Teen Drinking on Educational Attainment, NELS-88, Parameter Estimates and
Standard Errors
Covariates
High School
Completion College Entrance
Sophomore Year Senior Year
Drinker
(1)
Heavy Drinker
(2)
Drinker
(3)
Heavy Drinker
(4)
Drinker
(5)
Heavy Drinker
(6)
Indicators for age, race, and gender Ϫ.034
(.0048)
Ϫ.056
(.0063)
Ϫ.074
(.0096)
Ϫ.127
(.0101)
Ϫ.030
(.010)
Ϫ.076
(.0108)
Previous model and indicators for family income
and composition Ϫ.033
(.0048)
Ϫ.054
(.0062)
Ϫ.072
(.0092)
Ϫ.1156
(.0097)
Ϫ.043
(.0097)
Ϫ.079
(.0103)
Previous model and indicators for parental education Ϫ.033
(.0047)
Ϫ.053
(.0062)
Ϫ.067
(.0090)
Ϫ.1032
(.0094)
Ϫ.045
(.0094)
Ϫ.070
(.0099)
Previous model and school fixed effects Ϫ.035
(.0050)
Ϫ.051
(.0067)
Ϫ.078
(.0097)
Ϫ.114
(.0101)
Ϫ.063
(.0103)
Ϫ.088
(.0110)
Observations 9,946 10,833 9,913 10,849 9,439 9,895
Sample mean of education variable .941 .941 .367 .363 .397 .396
Sample mean of drinking variable .420 .236 .419 .236 .521 .288
Note.—NELS-88 p National Education Longitudinal Study of 1988. Heteroscedastic-consistent standard errors are reported in parentheses. Drinker
is a discrete variable that equals one for students who report having had a drink in the past month. A heavy drinker is someone who reports having had
five or more drinks in a row within the past 2 weeks.
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184 Dee/Evans
results indicate that students who reported drinking during their sophomore
year were about 3.5 percentage points less likely to complete high
school and 7.8 percentage points less likely to enter college. Sophomores
who drank heavily were over 5 percentage points less likely to complete
high school and roughly 11 percentage points less likely to enter college.
Seniors who drank were 3–6 percentage points less likely to enter college;
heavy drinkers were 7–9 percentage points less likely to enter college. All
of these estimated effects are statistically significant.
There is, however, reason to be concerned about whether the results
in table 1 represent a causal relationship. A central insight of the human
capital model (Becker 1964) is that the individual decision to acquire
schooling is an investment in future earnings potential. Accordingly, the
decision to acquire human capital should reflect the personal costs of
schooling as well as the discounted expected future benefits. Other things
being equal, students who find schooling unpleasant or who place little
value on the future earnings are more likely to drop out. Similarly, such
students may be more likely to engage in behaviors that might inhibit
their education or have adverse health consequences later in life. Because
these decisions are made simultaneously, OLS estimates like those presented
in the previous section may overestimate the true effect of teen
drinking on schooling outcomes.12
We can construct some direct evidence on whether drinking and schooling
are jointly dependent by exploring the timing of the teen decision to
drink. If teen drinking were truly independent of student achievement,
then the decision to drink as a senior should be unrelated to prior achievement
in the eighth and tenth grades. This hypothesis can be directly tested
with the NELS-88 data by estimating the “effect” of twelfth-grade drinking
in eighth- and tenth-grade test-score equations. However, the power
of this test is attenuated by the extent to which twelfth-grade drinking
is serially correlated with drinking that occurred in the eighth and tenth
grades. Therefore, this hypothesis was also tested among samples of students
who abstained from drinking and heavy drinking as sophomores.13
As eighth and tenth graders, NELS-88 respondents took tests in four
subject areas: reading, mathematics, science, and history. The standardized
scores on these four tests have been aggregated into eighth- and tenth-
12
This specification issue could alternatively be framed as a concern over unobserved
individual heterogeneity. Either formulation suggests that inferences based
on OLS estimates may falsely suggest that teen drinking reduces attainment. It
should be noted that it is also possible that the results in table 1 understate the
true effect of teen drinking on schooling. For example, this could occur if teen
drinking and dropping out of school constitute substitutable forms of teen
rebellion.
13
Questions about alcohol use were not asked of the eighth-grade respondents
to NELS-88.
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Teen Drinking and Educational Attainment 185
Table 2
OLS Estimates: The “Effect” of Twelfth-Grade Drinking on Eighth- and
Tenth-Grade Test Scores, NELS-88
Sample Selection by
Sophomore Drinking
Mean
Test
Score
Model 1 Model 2 No.
of
Obs.Drinker Heavy Drinker Drinker Heavy Drinker
Eighth grade–senior
panel:
All students 211 Ϫ2.7
(.8)
Ϫ9.7
(.8)
Ϫ3.9
(.8)
Ϫ9.3
(.8)
7,317
Not a drinker 212 Ϫ1.9
(1.0)
Ϫ10.5
(1.3)
Ϫ2.8
(1.1)
Ϫ10.0
(1.4)
4,237
Not a heavy drinker 214 Ϫ.5
(.9)
Ϫ8.6
(1.0)
Ϫ2.1
(.9)
Ϫ8.5
(1.0)
5,645
Sophomore–senior
panel:
All students 210 Ϫ3.2
(.7)
Ϫ10.1
(.8)
Ϫ4.6
(.8)
Ϫ9.8
(.8)
7,466
Not a drinker 212 Ϫ2.1
(1.0)
Ϫ10.0
(1.3)
Ϫ2.3
(1.1)
Ϫ9.7
(1.4)
4,334
Not a heavy drinker 213 Ϫ.7
(.8)
Ϫ8.1
(1.0)
Ϫ2.0
(.9)
Ϫ8.2
(1.0)
5,749
Note.—NELS-88 p National Education Longitudinal Study of 1988. Heteroscedastic-consistentstandard
errors are reported in parentheses. Model 1 includes indicators for race, gender, ethnicity, and year
of birth. Model 2 adds to model 1 school fixed effects and indicators for family composition, parental
education, and family income.
grade test scores for each student.14
Our samples of over 7,500 NELS-88
respondents consist of students who were enrolled in tenth grade in 1990,
in twelfth grade in 1992, who answered both drinking questions in 1990
and 1992, and who took all four tests in either the base year or the first
follow-up. Dropouts were omitted because their pattern of alcohol consumption
is likely to differ greatly from that of enrolled students. This
selection is not likely to generate any problematic bias for these stylized
evaluations since dropouts would tend to have lower test scores and a
higher prevalence of drinking.
The “effects” of twelfth-grade drinking on prior achievement are reported
in table 2. Drinking as a high school senior is always associated
with lower levels of prior achievement, even when other determinants of
student achievement are included as covariates. For example, drinking
heavily as a senior implies an eighth-grade test score that is roughly 10
points lower. This statistically significant reduction constitutes nearly 5%
of the mean test score and persists even when students who drank as
sophomores are excluded from the sample. The results for more moderate
twelfth-grade drinking and for the tenth-grade test scores demonstrate a
similar pattern: students who are doing poorly in school are more likely
14
The tenth-grade test score data should be interpreted with caution since student
performance on the eighth-grade test influenced the difficulty level of the
later NELS-88 tests.
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186 Dee/Evans
to drink later in high school. The timing and correlation of these decisions
raises serious doubts about the frequently cited conclusion that teen drinking
causes students to do poorly in school and about the appropriateness
of empirical designs that assume that teen drinking is determined independently
of student achievement.
III. Identifying Causal Effects
Although teens who drink are less likely to finish high school or start
college, the evaluations from table 2 have raised the critical concern that
teen drinking may proxy for some omitted factors in the educational
attainment equations. Generating unbiased estimates of the effect of teen
drinking on educational attainment requires an exogenous source of variation
in teen drinking. Following the work of Cook and Moore (1993),
we exploit the variation in teen alcohol use generated by relevant state
policies. There are two policy instruments that we can potentially use in
this manner: the MLDAs and state excise taxes on beer.
In 1977, 30 states had an MLDA of 18. By 1989, all states had raised
their MLDA to 21. The rapid change in state policy was precipitated in
part by passage of the Danforth-Lautenberg Act (PL98-363), signed on
July 17, 1984, which required the secretary of transportation to withhold
some federal highway funds from states that did not enact an MLDA of
21. In contrast to previous work, we examine the impact of the MLDA
on drinking using a within-group estimator where we effectively compare
the difference in drinking among high school seniors before and after
hikes in the MLDA to the contemporaneous changes among teens in
states with no reform. The need for a within-group model is strongly
suggested by the tremendous persistence in teen drinking and high school
graduation rates across states over time. If states with low graduation rates
had low MLDAs, a model that only examines cross-state variation would
overstate the reduced-form effect of alcohol availability and educational
attainment. These potential correlations can be eliminated from the data
by using panels of repeated cross-sections that allow us to include a
compete set of state and year fixed effects in the model. However, the
validity of this identification strategy also requires that the within-state
movement away from an MLDA of 18 was independent of teen drinking
(Besley and Case 1994; Meyer 1995). The fact that changes in the MLDA
were often compelled by federal law suggests that these changes were
exogenous. Additionally, in the next section, we also discuss some empirical
evidence that indicates that the timing of MLDA changes was
independent of state-specific trends in teen drinking. Because beer is the
drink of choice for most teens, within-state changes in beer taxes may
also provide the necessary variation in alcohol consumption to identify
the impact of drinking on educational attainment. However, as we illusThis
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Teen Drinking and Educational Attainment 187
trate in the next section, once we restrict our attention to models with
state fixed effects, excise taxes on beer appear to have no statistically
significant impact on teen alcohol consumption (Dee 1999b).
Our use of within-state variation in alcohol availability differs from
the work of Cook and Moore (1993) who used the cross-state variation
in MLDA and excise taxes on beer to identify the effect of teen drinking
on educational attainment. Their primary evidence of a link between
drinking and attainment are the results from reduced-form evaluations
that indicate there is a positive correlation between residing in a state with
a more restrictive drinking environment and subsequent educational attainment.
There is reason to be concerned that an identification strategy
based on the cross-state variation in such policies may be a poor one.
One immediate source of concern is that the magnitudes of the reported
effects are implausibly large.15
More generally, the potential difficulty with
state effects in conventional cross-sectional evaluations is that they may
be biased by unobserved and state-specific determinants of risky youth
behaviors and alcohol availability (e.g., cultural sentiment). To illustrate
this concern, we used the cross-sectional NELS-88 data presented in the
previous section to estimate reduced-form models for educational attainment
similar to those in Cook and Moore (1993). However, instead of
including state laws concerning alcohol availability, we added indicators
for state laws that should have no impact on educational attainment.16
These laws include the state excise taxes on cigarettes and gasoline,
whether the state had a death penalty, a waiting period for gun purchases
and a 65-mile-per-hour (MPH) speed limit.17
We estimated the “effect”
of these state policies on college entrance in probit models that included
demographic covariates as well as the indicators that reflect family income,
family composition, and parental education. In all cases, the state policies
correlated significantly with college entrance even though no plausible
causal relationship necessarily exists. For example, our evaluations suggest
that increases in cigarette taxes reduce the probability of entering college,
while higher gas taxes increase the probability (Dee and Evans 1997).
Furthermore, sophomores from states with a waiting period for gun pur-
15
This criticism is discussed in detail below.
16
For confidentiality reasons, the public-use version of the NELS-88 data set
does not contain state codes. However, through an agreement with the Department
of Education, we were able to match NELS-88 respondents to the state in which
they attended school in 1990.
17
The data on the level of beer taxes has been drawn from the Distilled Spirits
Industry Council of the United States (DISCUS 1996a) and has been converted
to real terms using the CPI ( ). Data on gas and cigarette taxes and1982–84 p 1
the death penalty are from the 1990–91 Book of the States. Data on speed limits
are from the Statistical Abstract of the United States. Data on waiting periods for
gun purchases are from the National Survey of State Laws.
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188 Dee/Evans
chases are 4.2 percentage points more likely to enter college, students
from states with a death penalty are 5.4 percentage points less likely to
enter college, and a 65-MPH speed limit implies a reduction of 8.8 percentage
points in the likelihood of entering college. All of these estimates
are statistically significant. The spurious cross-sectional correlation between
some state policies and the level of attainment raises doubt about
this widely employed identification strategy.
This study exploits the within-state variation in alcohol availability to
identify the effects of teen drinking on educational attainment. However,
a traditional instrumental variables (IV) estimator that adopts this approach
would require that we have repeated cross-sections that contain
data both on teens’ drinking and their subsequent schooling decisions.
Because this would imply either following cohorts of teens through their
early 20s or surveying individuals in their 20s and asking retrospective
questions about teen drinking, no large-scale nationally representative
survey has all the necessary information. To circumvent the lack of data,
we have relied on a new technique pioneered by Angrist and Krueger
(1992, 1995) that will allow us to generate instrumental variables estimates
using the cohort-specific information in two data sets.
A. Specifications
To illustrate how TSIV estimates are generated, consider the following
structural equation of educational attainment:
E p W p ϩ D g ϩ u ϩ v ϩ ␧ , (1)ist ist ist s t ist
where is Eist is an indicator for the education obtained by person i from
state s and birth cohort t; Wist is a vector of exogenous individual characteristics;
us and vt are state and cohort fixed effects; and ␧ist is a meanzero
random error. The potentially endogenous covariate of interest is an
indicator for teen drinking, Dist. The instrumental variable for Dist will be
an indicator, Mst, for whether a teen in a particular state and year cohort
was exposed to an MLDA of 18. Therefore, the model is exactly identified.
Most data sets that measure teen drinking do not follow these individuals
over time and record their ultimate level of education. As a result,
we typically do not have E, D, and M in the same data set.18
However,
the TSIV procedure requires only one data set with data on E and M and
a second data set with data on D and M for the same cohorts. Our firststage
data set, which has information on teen drinking and MLDA ex-
18
If all the necessary data were available in one data set, the appropriate specification
would be a bivariate probit. However, there is evidence that linear IV
estimation is a viable alternative to the bivariate probit model (Angrist 1991).
Furthermore, probit estimation of the first-stage and reduced-form equations
generate results similar to those reported for these linear specifications.
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Teen Drinking and Educational Attainment 189
posure, is based on pooled cross-sections from the MTF surveys. Our
second data set, which has information on educational attainment and
teen MLDA exposure, is based on the Census Bureau’s 5% 1990 PUMS.
These data sets are described in more detail in the next two sections.
The first step to calculating the TSIV estimate of g is to fit the models
for alcohol use with the MTF data and to use those parameter estimates
to predict the drinking behavior of the contemporaneous PUMS respondents.
Then, the TSIV estimate of g is generated by a regression of the
educational outcomes of the PUMS respondents on the cross-samplefitted
value for their alcohol use (Dee and Evans 1997). However, since this
model is just identified, the TSIV estimate of g is also fully implied by
the reduced-form evaluations with these two data sets. More specifically,
from the MTF data set, we can obtain an estimate of the first-stage relationship
between teen drinking and alcohol availability by estimating
the equation:
D p W p ϩ M g ϩ u ϩ v ϩ ␧ . (2)ist ist 1 ist 1t 1s 1t 1ist
From the PUMS data set, we can obtain an estimate of the reduced-form
relationship between educational attainment and the instrumental variable
by estimating the equation:
E p W p ϩ M g ϩ u ϩ v ϩ ␧ . (3)ist ist 2 st 2 2s 2t 2ist
Because our model is exactly identified, it is straightforward to show that
the TSIV estimate of g is equivalent to the ratio of the reduced-form and
first-stage estimates:
ˆ ˆ ˆg p g /g . (4)TSIV 2 1
This expression for the TSIV estimate of g proves useful for evaluating
the plausibility of prior estimates of the effect of teen drinking on educational
attainment and for placing bounds on the possible impact of state
alcohol policies on schooling decisions.
B. Sample Size
Another important specification issue concerns the appropriate sample
size that will allow us to construct meaningful inferences about the relationships
among teen drinking, a state’s MLDA, and educational attainment
within that state. In order to address this question, it is useful
to identify the likely magnitude of the reduced-form relationship between
a teen MLDA of 18 and attainment if it were the case that the OLS
estimates of the effect of drinking on attainment were unbiased. Consider
the case of heavy teen drinking. In the next section, we will demonstrate
that teen exposure to an MLDA of 18 increased heavy drinking among
students by a statistically significant 3.2 percentage points. The OLS esThis
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190 Dee/Evans
timates in table 1 indicated that heavy drinkers in tenth grade were 5.6
percentage points less likely to complete high school. If that were the
true effect, we would expect teen exposure to an MLDA of 18 to reduce
the probability of completing high school by only 0.18 percentage points
( ). Using heavy drinking in the twelfth grade, if the OLS.056 # .032
estimate were true, we would expect exposure to an MLDA of 18 to
reduce the probability of college entrance by 0.24 percentage points
( ). The precise estimation of such small effects is likely to.076 # .032
require a large data set.
To illustrate more carefully the necessity of having a large sample,
consider the following, bivariate regression model:
y p a ϩ bd ϩ ␧ , (5)i i i
where yi is an indicator that equals one if a student entered college and
di is an indicator for whether the student was a heavy drinker in high
school. Let zi denote the binary instrument for the respondent’s teen
exposure to an MLDA of 18. The IV or Wald (1940) estimate of b in this
equation is
¯ ¯(yFz p 1) Ϫ (yFz p 0)i iˆb p , (6)IV ¯ ¯( Fz p 1) Ϫ ( Fz p 0)d di i
where ( ) is the mean of yi for those observations with and¯yFz p 1 z p 1i i
other terms are similarly defined. The numerator and denominator capture
the reduced-form relationships between yi and zi and between di and zi.
Consider the case where OLS estimates of this simple model generate
unbiased estimates. Given these assumptions, it must be that a reducedform
regression of y on z would generate the following estimate:
ˆ ¯ ¯b p (y d z p 1) Ϫ (y d z p 0) p Ϫ.0024. (7)RF i i
This reduced-form estimate will only be statistically significant if:
ˆbRF
d d ≥ 1.96, (8)
ˆjRF
where is the standard error of . Under the assumptions we havej bRF RF
made, we can solve this expression for the minimum number of observations
that would be necessary to make such an inference about the
reduced-form relationship. Let and ,ˆ ˆ¯ ¯p p (yFz p 1) p p (yFz p 0)1 i 0 i
and suppose that there are n observations in both the treatment (z pi
) and the control ( ) groups. Therefore, approximately equals2
1 z p 0 ji RF
. Since , we can rewrite as2ˆ ˆ ˆ ˆ ˆ ˆ[p (1 Ϫ p ) ϩ p (1 Ϫ p )]/n p p p Ϫ .0024 j1 1 0 0 1 0 RF
. For equation (8) to be true, it must2ˆ ˆ ˆ[2(p Ϫ p ) Ϫ .0024(1.0024 Ϫ 2p )]/n0 0 o
be the case that .2 1/2ˆ ˆ ˆ.0024/{[2( p Ϫ p ) Ϫ .0024(1.0024 Ϫ 2p )]/n} ≥ 1.960 0 0
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Teen Drinking and Educational Attainment 191
Solving for n, we have that 2 2ˆ ˆn ≥ (1.96/.0024) [2(p Ϫ p ) Ϫ .0024(1.0024 Ϫ0 0
. Given a college entrance rate of 48% among the PUMS respon-ˆ2p )]0
dents, we can set . This calculation then implies that we wouldˆp p 0.480
need over 330,000 observations in the treatment group and an equal
number in the control group to generate a statistically significant
reduced-form relationship between college entrance and a teen MLDA
of 18. The reduced-form estimates we present in Section V are based
on samples of over 1.3 million individuals, and the calculations presented
here suggest that our samples are large enough to provide a fair test of
the hypothesis that alcohol availability has influenced educational attain-
ment.
The specification issues discussed in this section also provide a framework
for evaluating the plausibility of Cook and Moore’s (1993) widely
cited conclusion that teen exposure to an MLDA of 20 or 21 increased
the probability of completing college by 4.2 percentage points. One source
of concern is that the estimate is implausibly large. If we were to make
the very generous assumption that the same change in MLDA reduced
drinking by 5 percentage points, the implied effect of teen drinking on
college completion, using the Wald estimate, would be 84 percentage
points ( ). The implausibility of this implied IV estimate is another.042/.05
indication that an identification strategy based on cross-state heterogeneity
can be problematic. Furthermore, because these estimates are based
on fewer than 2,000 observations, the statistical significance of this estimate
may be driven solely by its unusually large magnitude.
IV. The First-Stage: The Impact of MLDA on Teen Drinking
This section presents estimates of the policy determinants of teen drinking
that are based on pooled cross-sections from the 1977–92 MTF
surveys.
A. 1977–92 Monitoring the Future
The widely used MTF surveys, which have been organized by the
Survey Research Center at the University of Michigan, were designed to
identify changes in important youth behaviors and attitudes. In the spring
of each year, a nationally representative cross-section of high school seniors
have been asked about their drug and alcohol use. These samples
have been constructed in three stages. The first stage consisted of selecting
geographic areas. The basis for these selections were the primary sampling
units (PSU) developed by the Survey Research Center for nationwide
interviews. In the second stage, high schools within each PSU were chosen.
The probability of selection for a school was proportional to the size of
its senior class. In the final stage, up to 400 seniors in a selected school
are included in the data collection. In small schools, all seniors were
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192 Dee/Evans
usually interviewed. In larger schools, a sample of seniors was randomly
selected. Each yearly survey has consisted of at least 15,000 respondents
from roughly 130 schools.
For confidentiality reasons, the public-use MTF data do not identify
the state in which the selected school is located. In order to match the
teen drinking behavior reported in the MTF surveys to state alcohol
policies, we have reached a special agreement with the Survey Research
Center. As a condition of this agreement, we could only match MTF
respondents to their states by accepting some limitations on the available
demographic covariates. The data set we received identified the proportion
of respondents satisfying three drinking definitions within a given state,
year, race, and age cell and the number of observations within that cell.
More specifically, responses with a given state and year were defined by
gender, age (i.e., above or below the age of 18), and race/ethnicity (i.e.,
white non-Hispanics or not). This data set contains 3,941 cells representing
the responses of 255,560 students in 44 states.19
Since evaluations
with these data replicate prior results, this modest aggregation does not
appear to generate any bias.
This data set contains three distinct measures of teen drinking participation.
As in the NELS-88 data, a drinker is a respondent who reports
having had a drink in the last month. A heavy drinker has had five or
more drinks in a row in the last 2 weeks. Additionally, this unique data
set identifies “moderate drinkers”: those who report having had 10 or
more drinks within the past month. Each level of teen drinking has been
characterized by a slow but steady decline over the 1977–92 period. However,
this trend has reversed in recent years and the rates at which teens
use and abuse alcohol are still among the highest of any segment of society
(Grant et al. 1991; Johnston et al. 1999).
B. Alcohol Availability
The policy variables of interest in this literature have been those that
affect the availability of alcohol: the MLDAs and taxes. Information on
the history of alcohol taxation and MLDA in the states has been taken
from two publications of DISCUS (1996a, 1996b). Since some changes
in MLDA occurred midyear, the MLDA for a state in a given year is
considered to be the one in effect for the largest proportion of that year.
Like much of the prior research, we also focused on federal and state
19
Cells with fewer than five respondents were deleted by the Survey Research
Center. The public use surveys over the 1977–92 period consisted of 271,012
respondents. Not all of the 44 states in this data set are represented in each survey
year.
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Teen Drinking and Educational Attainment 193
excise taxes on the drink of choice among teens, beer.20
The beer taxes
have been defined per gallon of beer and, where relevant, refer to the tax
on beer greater than 3.2% alcohol by volume or sold in cases. The nominal
taxes have been converted into real terms using the Consumer Price Index
( ).1982–84 p 1
Each of these policy instruments has exhibited considerable variation
over this period. In 1977, 30 states had an MLDA of 18, and nearly 60%
of the MTF respondents resided in these states. By the end of 1988, all
states had raised their MLDA to 21. However, over this period, the
amount of beer tax variation that can be understood as unique withinstate
innovations is actually quite limited. In general, the real value of
beer taxes was declining over much of this period due to the shared effects
of price inflation. The one exception to this time-series trend was the
1991 increase in the federal tax on beer. The relatively stable cross-state
differences in beer taxes are quite large and have been exploited in prior
studies (Grossman, Coate, and Arluck 1987; Coate and Grossman 1988;
Grossman, Chaloupka, et al. 1993; Grossman, Sindelar, et al. 1993; Kenkel
1993; Cook and Moore 1994). However, an important concern raised here
and elsewhere (Dee 1999b) is that this cross-sectional beer tax variation
may be correlated with the unobserved state-specific determinants of
youth behaviors. The unique within-state variation in beer taxes that is
available to us is driven by state changes in their nominal excise taxes on
beer. Of the 44 states represented within our MTF data set, 19 changed
their beer taxes over periods in which students were interviewed. While
this tax variation is relatively limited, Dee (1999b) shows that there is
enough variation to demonstrate that the within-panel tax elasticities are
smaller and statistically distinguishable from the conventional cross-sectional
elasticities.
C. Results
The evaluations we report here are based on weighted OLS regressions
in which the dependent variable is the proportion of students within a
cell who satisfy a drinking definition and the weight is the number of
observations per cell.21
All of these models condition on the available
demographic information and fixed effects for each of the annual survey
cohorts. We present some results based on the full 1977–92 MTF data set
in order to capture all of the relatively limited within-state variation in
20
Some of the earlier research used price data. However, changes in the tax
provide an independent source of variation in the price of alcohol and are less
subject to measurement error. There is evidence that tax increases on alcohol are
completely passed on to consumers in the form of higher prices (Cook 1981).
21
This weighted linear specification utilizes the data as we received them and
provides a plausible correction for heteroscedasticity. However, as the evaluations
in Sec. V demonstrate, these results are quite robust to other specifications.
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194 Dee/Evans
Table 3
Weighted Least Squares Estimates of the Determinants of Alcohol Use by
Teens, Monitoring the Future, 1977–92: Parameter Estimates and
Standard Errors
Independent
Variable
With Cohort Fixed Effects With State and Cohort Fixed Effects
1977–92
(1)
1977–92
(2)
1977–86
(3)
1977–86
(4)
1977–92
(5)
1977–92
(6)
1977–86
(7)
1977–86
(8)
Drinking:
MLDA 18 .073
(.005)
.041
(.005)
.040
(.006)
.034
(.005)
.035
(.006)
.035
(.006)
.054
(.009)
.038
(.006)
MLDA 19 .027
(.005)
.009
(.005)
.009
(.006)
. . . Ϫ.001
(.006)
Ϫ.001
(.006)
.019
(.008)
. . .
MLDA 20 .072
(.010)
.056
(.010)
.056
(.010)
. . . .005
(.011)
.005
(.011)
.012
(.013)
. . .
Real beer tax Ϫ.184
(.010)
. . . . . . . . . Ϫ.001
(.030)
. . . . . . . . .
Moderate
drinking:
MLDA 18 .033
(.003)
.026
(.003)
.026
(.003)
.025
(.003)
.020
(.004)
.021
(.004)
.035
(.006)
.023
(.004)
MLDA 19 .004
(.003)
Ϫ.001
(.003)
Ϫ.0002
(.003)
. . . Ϫ.002
(.004)
Ϫ.002
(.004)
.015
(.005)
. . .
MLDA 20 .021
(.006)
.017
(.006)
.016
(.006)
. . . Ϫ.005
(.007)
Ϫ.005
(.007)
Ϫ.0004
(.009)
. . .
Real beer tax Ϫ.044
(.006)
. . . . . . . . . .010
(.019)
. . . . . . . . .
Heavy drinking:
MLDA 18 .049
(.005)
.028
(.005)
.027
(.005)
.025
(.005)
.026
(.006)
.027
(.006)
.042
(.009)
.032
(.006)
MLDA 19 .008
(.005)
Ϫ.004
(.005)
Ϫ.005
(.005)
. . . Ϫ.009
(.006)
Ϫ.008
(.006)
.011
(.008)
. . .
MLDA 20 .064
(.009)
.053
(.009)
.051
(.009)
. . . .004
(.011)
.004
(.011)
.008
(.012)
. . .
Real beer tax Ϫ.124
(.009)
. . . . . . . . . .037
(.028)
. . . . . . . . .
Note.—Drinking sample mean p .657; moderate drinking sample mean p .138; heavy drinkingsample
mean p .367. Standard errors are reported in parentheses. All models include binary indicators forgender,
age, and race. The 1977–92 evaluations are based on 3,941 cells representing the responses of 255,560
Monitoring the Future (MTF) respondents. The 1977–86 evaluations are based on 2,511 cells representing
the responses of 163,177 MTF respondents. The weight is the number of respondents per cell.
beer taxes. However, we also report results based only on the 1977–86
MTF data set, which has drinking data for those cohorts whose subsequent
educational outcomes we observe in the 1990 PUMS data. In table 3, we
present the key results from estimating the determinants of teen participation
in each of the three drinking measures. The top panel has the
results for drinking participation; the middle and bottom panels report
the results for moderate and heavy drinking, respectively. The unreported
coefficients on the demographic covariates generally indicate that older,
white males are more likely to drink alcohol.
The first four models in table 3 parallel the prior literature by estimating
the effects of the cross-state variation in alcohol policies on each drinking
measure. These models uniformly indicate that exposure to an MLDA of
18 implies a significantly higher prevalence of each teen drinking behavior.
Furthermore, model 1 also replicates the traditional result that students in
states with high beer taxes are substantially less likely to drink. The implied
tax elasticities of these teen drinking measures are quite large. For example,
the implied elasticity of heavy teen drinking with respect to the beer tax is
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Teen Drinking and Educational Attainment 195
Ϫ0.17 . The magnitude of this elasticity is consistent(Ϫ.124 # [.50/.367])
with the findings of other research that has used the cross-state variation
in taxes (Leung and Phelps 1993). However, one suggestive indication that
these cross-sectional results should be viewed with some suspicion is the
evidence that exposure to an MLDA of 20 was also associated with a
significantly higher prevalence of these drinking behaviors.
We provide more definitive evidence on the relevance of these specification
concerns in the last four models, which introduce state fixed
effects that control for the unobserved, state-specific determinants of these
drinking behaviors. The estimates from model 5 demonstrate that the
frequently cited correlation between the cross-state variation in beer taxes
and teen drinking does not appear to be robust. The within-state variation
in beer taxes exhibits a small and statistically insignificant correlation with
each teen drinking measure. Furthermore, model 3 indicates that students
facing an MLDA of 19 or 20 were, in general, no more likely to consume
alcohol than students facing an MLDA of 21.22
However, the movement
away from an MLDA of 18 did have a significant impact. In particular,
model 8 indicates that students who faced an MLDA of 18 were 3.8
percentage points more likely to drink, 2.3 percentage points more likely
to drink moderately, and 3.2 percentage points more likely to drink
heavily.
The lack of a correlation between the within-state variation in beer
taxes and teen drinking is straightforward evidence of the limitations of
conventional identification strategies based on cross-state variation. However,
one important concern with this unorthodox result is that it might
simply be driven by the collinearity between the state effects and the beer
taxes. As a check of this possibility, we have replicated the results from
table 3 using only those respondents in the 19 states that exhibited withinstate
variation in their beer taxes. The results of those evaluations, which
were based on the responses of 133,854 students, were quite similar.23
Nonetheless, the fact that beer taxes have no statistically significant impact
on teen drinking may appear to some to be completely inconsistent with
most prior research. However, almost all prior demand estimates based
on individual-level data for teens have relied solely on the cross-state
variation in taxes to identify the parameters of interest. Recent studies
that employ the within-state variation in beer taxes as the identifying
22
The one exception is that an MLDA of 19 had a weakly significant effect on
drinking participation. The irrelevance of higher MLDA is not entirely surprising
in this context since only an MLDA of 18 makes alcohol available to some high
school age students.
23
Dee (1999b) presents additional evidence that the collinearity between beer
taxes and state fixed effects is not problematic. For example, even in the models
that include state fixed effects, the standard error on the estimated tax responsiveness
of teen drinking is still small enough to reject the conventional estimate.
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196 Dee/Evans
assumption generate results similar to those reported here (Dinardo and
Lemieux 1996; Dee 1999b).
There are, however, numerous papers that examined the link between
beer taxes and highway traffic fatalities using panel data and state fixed
effects. In the majority of these papers, the authors find that beer taxes
reduce alcohol-related traffic fatalities.24
Two points about this body of
research are worth noting. First, in a related paper, Dee (1999b) shows
that the tax effect in teen auto fatality models is not robust to the inclusion
of state-specific time trends.25
Including state-specific time trends may be
particularly important in this context since a large portion of the withinstate
changes in tax rates is due solely to inflation rather than changes in
the nominal tax rates. Interestingly, the effect of the MLDA in these
models is quite robust across specifications. Second, the estimates in these
traffic studies are implausibly large. For example, Saffer and Grossman
(1987) estimate that the elasticity of traffic fatalities for 18–20-year-olds
with respect to beer tax is Ϫ0.17, but since beer taxes represent roughly
10% of the retail price, this implies a price elasticity of about Ϫ1.7 (Ϫ0.17/
.10). Since alcohol is a factor in about half of traffic safety fatalities, this
suggests that the elasticity of alcohol-sensitive traffic fatalities with respect
to price is about Ϫ3.4. If these conventional estimates are accurate, a mere
3% increase in the price of beer would reduce youth fatalities by more
than the move to an MLDA of 21 has (Dee 1999b).
The empirical models presented here indicate that beer taxes do not
provide a plausible instrument for teen drinking. However, the movement
away from an MLDA of 18 does appear to provide a valid source of
exogenous variation for identifying the welfare consequences of teen drinking.
The evaluations reported in table 3 indicate that an MLDA of 18 had
a large and statistically significant impact on all levels of teen drinking. An
important concern with these evaluations is whether they identify the independent
effect of MLDA changes on teen drinking. If the timing of a
state’s MLDA change were also a response to a change in teen drinking,
the quality of our identification strategy would be in doubt (Besley and
Case 1994; Meyer 1995). However, in addition to the available anecdotal
evidence, there is some suggestive empirical evidence to buttress the assumption
that the variation in state MLDA was independent of teen drinking.
The national trends in all levels of teen drinking were quite stable in
the period before the dramatic MLDA changes. This suggests that the
movement away from an MLDA of 18 was not a response to increases in
24
For an overview of the literature on youth traffic safety, see Dee and Evans
(2001).
25
The implausibility of the conventional tax results is more convincingly indicated
by a counterfactual based on comparing models of nighttime fatalities to
models of daytime fatalities that have substantially lower rates of alcohol involvement
(Dee 1999b; Dee and Evans 2001).
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Teen Drinking and Educational Attainment 197
teen drinking. More formally, the first-stage coefficients reported in table
3 are largely robust to the inclusion of both linear and quadratic statespecific
trend variables, implying that the state-specific variation in teen
drinking was not correlated with the timing of a state’s MLDA change.26
Also, the results presented in table 3 indicate that the correlation between
an MLDA of 18 and each level of teen drinking is roughly the same regardless
of whether state fixed effects are included. The weak relevance of
the considerable cross-state heterogeneity in this instance suggests that
within-state heterogeneity is unlikely to be problematic.
V. Reduced-Form and Two-Sample Instrumental
Variables Estimates
The evaluations in the previous section demonstrated that the timing
of a state’s movement away from an MLDA of 18 had a significant impact
on all levels of teen drinking. It follows that if teen drinking had an
independent effect on schooling decisions, then changes in MLDA should
have also had an effect on educational attainment. The evaluations presented
in this section address this question directly by estimating the effect
of teen exposure to an MLDA of 18 on high school completion, college
entrance, and college completion.
A. 1990 Public-Use Microdata Sample
In Section III we demonstrated that, because the effect of teen exposure
to an MLDA of 18 may be quite small, a precise estimate of its effect is
likely to require a large number of observations. Therefore, we have used
data from the Census Bureau’s 1990 5% PUMS to estimate the impact
on educational attainment of teen exposure to an MLDA of 18.27
The
1990 PUMS consists of the more than 12 million individual respondents
who received the long-form questionnaire in that census enumeration.
Our PUMS sample consists of white, black, and Hispanic respondents
from the 1960–69 birth cohorts. These respondents ranged in age from
21 to 30 at the time of the 1990 interview. Their MLDA exposure at age
17 occurred during the 1977–86 period when many state MLDAs were
being increased. Educational attainment for these respondents has been
defined by binary indicators for high school completion, college entrance,
and college persistence. In the PUMS data set, high school completion
includes those who have earned equivalency degrees. College entrants
26
We have also regressed an indicator for an MLDA of 18 on state effects,
cohort effects, and the level of teen drinking lagged by 2 and 3 years. The lack
of a partial correlation between lagged teen drinking and a state’s MLDA status
is further evidence that the instrument is exogenous.
27
We have replicated the high school completion results to be reported here
with a sample of 19–21-year-olds from the 1981–92 October Current Population
Survey (CPS). However, that data set only consisted of 67,361 respondents.
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198 Dee/Evans
have been defined as those respondents who have completed “some college”
or earned a bachelor’s degree.28
Because some of the younger respondents
in this sample have not had a chance to have a “completed
spell” of college completion, college persistence has been defined to include
those who are still enrolled in a college program in addition to
those who have earned a bachelor’s degree.29
The members of this PUMS sample were matched to the MLDA in
their state of birth when they were 17. Because some respondents dropped
out of school before their MLDA exposure at age 17, only students who
attained at least the eleventh grade are included. This construction allows
the PUMS sample to roughly parallel the contemporaneous MTF sample
whose first-stage assignments and drinking behavior we observe. However,
it should be noted that these data limitations imply that we cannot
speak directly to the drinking and education relationship for earlier dropouts.
The final PUMS sample consists of 1,376,762 respondents. Matching
these respondents to their teen MLDA by their states of birth does not
appear to be problematic. Tabulations from the 1980 PUMS indicate that
nearly 80% of teens resided in their state of birth. Furthermore, there is
no reason to believe that the pattern of interstate childhood mobility for
those who advanced past the tenth grade was correlated with changes in
MLDA. A specification check based on constructing mobility-adjusted
measures of teen MLDA exposure offers further evidence that this construction
is not misleading (Dee and Evans 1997).
B. Reduced-Form Estimates
We estimated the effects of teen exposure to a relaxed drinking environment
on educational attainment using linear probability models and
heteroscedastic-consistent standard errors. However, similar results
emerged from evaluations based on probit and logit specifications. The
results of estimating the impact of an MLDA of 18 on high school completion,
college entrance, and college persistence are reported in table 4.
These models consistently demonstrate that non-Hispanic whites are significantly
more likely to continue their schooling while males are less
likely. The first three models reported in table 4 include cohort fixed
effects but not state fixed effects. These estimates indicate that, even in
the absence of controls for unobserved state heterogeneity, there is no
evidence that teen exposure to an MLDA of 18 reduced subsequent educational
attainment. In fact, these specifications indicate that the cross-
28
This definition excludes those who earn an associate’s degree. However, this
construction does not substantively alter the pattern of the results.
29
Again, this definition is not problematic. Similar results are obtained using
cohorts with completed spells and defining college completion as having earned
a bachelor’s degree.
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Teen Drinking and Educational Attainment 199
Table 4
Reduced-Form Linear Probability Models: The Determinants of Educational
Attainment, 1990 PUMS, Ages 21–30
Covariates
With Cohort Fixed Effects
With State and Cohort
Fixed Effects
High School
Completion
College
Entrance
College
Persistence
High School
Completion
College
Entrance
College
Persistence
MLDA of 18
at age 17 .00115
(.00051)
.00074
(.00099)
.00812
(.00090)
Ϫ.00099
(.00081)
.00198
(.00156)
.00095
(.00144)
White nonHispanic
.08597
(.00084)
.09702
(.00121)
.12377
(.00102)
.07937
(.00086)
.10118
(.00127)
.12288
(.00107)
Male Ϫ.01750
(.00044)
Ϫ.02631
(.00085)
Ϫ.01353
(.00078)
Ϫ.01763
(.00044)
Ϫ.02665
(.00085)
Ϫ.01385
(.00078)
R-squared .0143 .0051 .0122 .0173 .0126 .0196
Note.—Heteroscedastic-consistent standard errors are reported in parentheses. This data set contains
1,376,762 observations.
state variation in teen exposure to a relaxed drinking environment is positively
and significantly correlated with both high school completion and
college persistence.30
The next three models in table 4 condition on unobserved state-specific
determinants by introducing state fixed effects. Using the restricted and
unrestricted R-squared from these evaluations, it is straightforward to
show that the state fixed effects are statistically significant determinants
of educational attainment.31
However, these models imply that the withinstate
variation in the MLDA over time has had small and statistically
imprecise effects on all three measures of attainment. Only the coefficient
in the high school completion model has the negative sign that would be
expected if one believed alcohol availability and teen drinking actually
reduced educational attainment. And that effect is relatively small (less
than one-tenth of a percentage point).
C. Two-Sample Instrumental Variables Estimates
First-stage estimates indicate that exposure to an MLDA of 18 had a
significant impact on all levels of teen drinking (table 3). However, the
30
However, evaluations with these data can replicate Cook and Moore’s (1993)
NLSY-based result that teen residence in a state with a high MLDA and college
completion are positively correlated. Conditional on other covariates, PUMS respondents
who were 17 in 1981 and 1982 in a state with an MLDA of 20 or 21
were more likely to complete college.
31
For example, using the high school completion evaluations, the test value for
an F-statistic is , which[(.017327 Ϫ .014259)/50]/[(1 Ϫ .017327)/1,376,700] p 86
exceeds the standard critical values for an F-statistic. The hypothesis that the state
effects have zero coefficients is rejected. The state effects are jointly significant in
the other models as well.
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200 Dee/Evans
reduced-form estimates presented above indicate that alcohol availability
had small and insignificant effects on educational attainment (table 4). The
TSIV procedure developed by Angrist and Krueger (1992, 1995) will allow
us to tie these results together by generating unbiased estimates of the
effect of teen drinking on educational attainment that can be compared
to some of the OLS estimates presented in table 1.
The TSIV estimates reported here have been based on a cross-sample
matching of the 1977–86 MTF surveys and the PUMS respondents who
were 17 over the same period. More specifically, these data sets have been
matched by state, year, race, and gender indicators.32
For purposes of this
procedure, the MTF data on teen drinking behavior within the state/year/
race/sex cells were converted back to their original status as 163,177 individual-level
records. Because some of the MTF cells were empty, the
number of PUMS respondents has fallen to 1,319,806. As discussed in
Section III, the first step in the construction of the TSIV estimates was
to form cross-sample fitted values for teen drinking using first-stage coefficients
based on the MTF data and the teen MLDA exposure of respondents
in both data sets. Then, consistent second-stage estimates can
be produced by regressing the educational outcomes of the PUMS respondents
on these cross-sample fitted values.
The results of these evaluations are reported in table 5. The first panel
of table 5 reports the effect of an MLDA of 18 on each measure of teen
drinking. These estimates are consistent with the results reported earlier:
exposure to an MLDA of 18 implies significantly higher probability of
participation in each teen drinking measure. The second panel of table 5
reports the effect of an MLDA of 18 on each measure of attainment.
These estimates also replicate the results discussed in the previous section:
teen exposure to an MLDA of 18 had small and statistically insignificant
effects on educational attainment. The final panel of table 5 contains the
TSIV estimates of the effect of teen drinking on educational attainment.
Note that each TSIV estimate is equivalent to the ratio of the reducedform
and first-stage coefficients. The effects of teen drinking on college
entrance and on college completion are positive and statistically insig-
nificant.33
This suggests that the covariance between teen drinking and
32
Since the MTF respondents are not all 17 years old, there are some caveats
associated with this matching. However, the resulting TSIV estimates are consistent
with the patterns established by the reduced-form estimates.
33
Standard errors were computed under the assumption of zero covariance
between the first-stage and reduced-form estimates using a linear Taylor series
approximation. Using these assumptions, it is straightforward to show that the
t-statistic for the TSIV estimates is a function of the t-statistics in the first-stage
and reduced-form evaluations. Because the first-stage estimates are precise, the
TSIV t-statistics approximate those in the reduced-form evaluations.
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Table 5
TSIV Estimates of the Effect of Teen Drinking on Educational Attainment, 1977–86
TSIV Estimates
First-Stage Estimates, 1977–86 MTF Reduced-Form Estimates, 1990 PUMS
Dependent Variable
Endogenous Covariate
Dependent Variable
Effect of an
MLDA of 18 Dependent Variable
Effect of an
MLDA of 18 Drinker
Moderate
Drinker
Heavy
Drinker
Drinker .03813
(.00405)
High school completion Ϫ.00078
(.00083)
High school completion Ϫ.021
(.022)
Ϫ.034
(.035)
Ϫ.024
(.026)
Moderate drinker .02334
(.00334)
College entrance .00183
(.00159)
College entrance .048
(.042)
.078
(.068)
.057
(.049)
Heavy drinker .03215
(.00435)
College persistence .00134
(.00146)
College persistence .035
(.038)
.057
(.063)
.042
(.046)
Number of observations 163,177 Number of observations 1,319,806 Number of observations 1,319,806 1,319,806 1,319,806
Note.—TSIV p two-sample instrumental variables; MTF p Monitoring the Future; PUMS p Public-Use Microdata Sample; MLDA p minimum legal drinking
age. Heteroscedastic-consistent standard errors are reported in parentheses. All models include state, cohort, race, and sex fixed effects.
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202 Dee/Evans
discontinued schooling, identified in table 1 and in prior studies, does
not represent a causal effect.
However, the TSIV estimates suggest that teen drinking may reduce
the probability of completing high school. For example, they indicate that
drinkers are 2.1 percentage points less likely to complete high school,
moderate drinkers are 3.4 percentage points less likely, and heavy drinkers
are 2.4 percentage points less likely. These effects are smaller than the
corresponding OLS in table 1, and each is statistically insignificant. Do
these results imply that the estimates in table 1 overstate the true effect
or that there simply was insufficient power in the instrumental variable
to identify the true effect? One way to address this question is to ask
whether the TSIV estimates would have been significant if they were equal
in magnitude to the estimates in table 1. For example, if the TSIV estimate,
like the estimate in table 1, found that heavy drinking reduced the probability
of high school completion by 5.2 percentage points, the t-statistic
would have had an absolute value of 2. These simple calculations suggest
that if teen drinking did have a significant effect on high school completion,
the TSIV procedure and an identification strategy based on the
within-state variation in MLDA would have had sufficient power to distinguish
it. However, the imprecision of the reduced-form and TSIV estimates
does qualify the high school completion results somewhat. In
particular, the 95% confidence interval for the TSIV estimate of this effect
does include the marginal effect reported in table 1. However, it should
be noted that these evaluations also have less relevance for high school
completion since the MTF data only allow us to identify the first-stage
drinking responses of high school seniors.
The results in table 5 make a compelling case that the lower educational
attainment of teenagers who drink may in the end simply reflect correlation
rather than causation. In cases where a direct comparison is possible,
the TSIV estimates are smaller than the corresponding OLS values. More
specifically, the only two groups of OLS and TSIV estimates that we can
directly compare are the effects of drinking and heavy drinking in the
twelfth grade on college entrance.34
Although the TSIV estimates of these
effects in table 5 are statistically insignificant, these estimates are still
sufficiently precise to reject the null hypothesis that the TSIV and OLS
estimates are equal. Looking at the final rows of table 1, drinking is
estimated to decrease college entrance by 6.3 percentage points. The 95%
confidence interval for this estimate is (Ϫ0.083, Ϫ0.043). In comparison,
the confidence interval for the corresponding estimate in table 5 is
(Ϫ0.034, 0.130). Likewise, OLS estimates suggest that twelfth-grade heavy
drinking decreases the chance of enrolling in college by 8.8 percentage
34
Because of the sample selection rules, the results in table 1 for high school
completion use tenth-grade drinking as the covariate of interest.
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Teen Drinking and Educational Attainment 203
points with a 95% confidence interval of (Ϫ0.110, 0.066). The confidence
interval for this parameter in the TSIV models is (Ϫ0.041, 0.155).
In this instance, the statistical insignificance of the basic reduced-form
relationship between the MLDA 18 and educational attainment is also
informative. As we mentioned above, some authors have suggested that
education outcomes can be improved by changing the policies concerning
alcohol availability. For example, Cook and Moore (1994, p. 568) state
that “increasing the tax on beer and other alcoholic beverages can be
justified by the potential benefits associated with reduced violent crime
and traffic accidents and improved school performance.” Our results suggest
that these gains will be incredibly small, if they exist at all. Using
the results from table 4, and constructing a 95% confidence interval
around the estimates for the MLDA of 18 coefficient, we find that raising
an MLDA from 18 to 21 would increase the probability of graduation
by at most 0.3 percentage points and increase college entrance rates by
at most 0.1 percentage points. Because we cannot even detect a basic firststage
relationship between changing taxes and teen drinking, there is no
evidence to suggest that higher beer taxes can be used to improve educational
outcomes.
D. Specification Checks
The estimates presented in tables 4 and 5 provide novel evidence on
the relationship between alcohol policies, alcohol use, and educational
attainment. We have evaluated the robustness of these results by examining
the reduced-form relationship between teen MLDA exposure and subsequent
educational attainment in more detail. For example, we have constructed
one important check of these reduced-form results by exploring
the relationship between an earlier episode of MLDA variation and educational
attainment (Dee and Evans 1997). More specifically, we have
replicated the evaluations in table 4 with the 1950–59 birth cohorts in the
1990 PUMS. Several of these cohorts who were 17 between 1967 and
1976 were exposed to reductions in state MLDA as teens. The construction
of this PUMS sample was similar to that of the younger PUMS
cohorts. An added feature of working with these earlier cohorts is that,
since they were between 31 and 40 at the time of the 1990 interview, they
had largely completed their spells of schooling. Therefore, we have defined
college completion for these cohorts as simply having a bachelor’s degree.
Reduced-form estimates with these cohorts indicate that the effect of teen
exposure to a relaxed drinking environment on subsequent educational
attainment was also small and statistically insignificant.
Another specification concern involves the fact that some of the
younger 1990 PUMS respondents may not have finished entering and
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204 Dee/Evans
completing college when interviewed.35
This “completed spells” problem
could confound the reduced-form evaluations presented in table 4 if state
and cohort-specific patterns of schooling completion are related to the
timing of the within-state changes in MLDA. The reduced-form evaluations
with the older PUMS cohorts suggest that the patterns of incomplete
spells are not generating any bias in the results reported in table 4.
Nonetheless, we also replicated the reduced-form evaluations with samples
that incrementally exclude the younger cohorts (Dee and Evans 1997).
These evaluations generate results similar to those in table 4: teen exposure
to an MLDA of 18 had small and insignificant effects on all three measures
of educational attainment.
A related specification issue concerns omitted variable biases. These
evaluations have included only those demographic covariates that are unarguably
exogenous. A great deal of research (Hanushek 1986; Haveman
and Wolfe 1995) has indicated that other teen characteristics like family
structure, family income, and parental education are strong correlates of
student achievement. Unfortunately, such data are unavailable in the
PUMS. However, since there is no reason to believe that within-state
trends in these attributes correlate with the timing of MLDA changes, it
is unlikely that the omission of these attributes generates any bias in the
parameter of interest. Nonetheless, we also evaluated specifications that
introduced controls for the within-state variation in these attributes (Dee
and Evans 1997). Data on these family characteristics were constructed
for households with teenage children enrolled in school using the October
CPS from these years. Because local macroeconomic conditions might
also affect schooling decisions (Duncan 1965), the state unemployment
rate at age 17 has also been included as a covariate. The inclusion of these
covariates as well as race- and gender-specific cohort effects did not substantively
alter the results presented in table 4.
Other important specification checks concern the appropriateness of
matching respondents by their state of birth to an MLDA of 18 at age
17. Since most teens reside in their state of birth and because there is no
reason to believe that childhood mobility is correlated with the timing of
MLDA changes, this approach should not be problematic. Nonetheless,
we addressed this concern by forming a weighted MLDA that reflects
the pattern of teen mobility observed over the period in question. Using
the 1980 5% PUMS, the probabilities a teen born in a particular state
resided in a particular state were constructed. These were then used to
adjust the teen exposure to an MLDA of 18. Card and Krueger (1992)
employed a similar adjustment in their research on school quality and
expenditures. Evaluations with the mobility-adjusted MLDA variable are
also consistent with the results presented in table 4 (Dee and Evans 1997).
35
Angrist and Evans (1999) discuss this issue in more detail.
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Teen Drinking and Educational Attainment 205
Evaluations with the mobility-adjusted MLDA variable also suggest
that the general measurement error in teen MLDA exposure introduced
by the state-of-birth match is not problematic. The presence of measurement
error implies that the coefficient on the MLDA variable may
be attenuated (i.e., biased toward zero). It is also important to note that
such an occurrence could only be an important issue for the high school
completion model. If the coefficients in the college entrance or persistence
models were attenuated, it would only mean that the true coefficients
were even more positive. However, attenuation in the high school completion
model could mean that the true effect of an MLDA of 18 was
more negative than that reported in table 4. As an additional specification
check, we have matched the five birth cohorts who were 21–25 at the
time of the 1990 interview to their MLDA exposure at age 17 using their
reported state of residence in 1985 rather than their state of birth. The
reduced-form evaluations with this sample suggest that a teen MLDA of
18 had a positive and statistically insignificant effect on high school completion.
This sample consisted of over 620,000 respondents and had considerable
within-state variation in MLDA. Among those who were 17 in
1982, nearly 34% were exposed to an MLDA of 18. Among those who
were 17 in 1986, only 5% were exposed to an MLDA of 18.
VI. Conclusions
Though alcohol use is illegal for teens in the United States, its abusive
consumption is surprisingly common, with roughly a third of high school
seniors self-identifying as heavy drinkers. This abusive drinking can promote
a broad variety of risks to the welfare and development of teens,
perhaps most notably, traffic-related accidents and fatalities (Dee and
Evans 2001). However, previous research has suggested that reduced educational
attainment also represents an important consequence of teen
drinking and that reductions in teen alcohol availability can therefore
improve student outcomes. The evaluations presented in this article have
raised two concerns about those conclusions. One is that the correlation
between student outcomes and teen drinking may not reflect a causal
relationship. The second concern is that the frequently employed identification
strategy based on the cross-state variation in alcohol control
policies may not be appropriate. The evidence presented here suggests
that, to some extent, both concerns are empirically relevant. For example,
estimates of the policy determinants of teen drinking demonstrated that,
though the cross-state variation in beer taxes correlates with teen drinking,
the within-state variation does not. Therefore, frequent recommendations
for increased beer taxes appear to be based on what may only be a spurious
correlation generated by unobserved state heterogeneity. However, the
within-state increases in MLDA, which significantly affected all levels of
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206 Dee/Evans
teen drinking, provided a source of exogenous variation for identifying
the true effect of teen alcohol consumption on educational attainment.
The TSIV estimates based on this instrument suggest that teen drinking
has not had an independent effect on any level of educational attainment.
By focusing on the magnitudes of the links among alcohol policy, teen
drinking, and educational attainment, this identification strategy has also
underscored the fact that alcohol control policies could at best be a fairly
weak policy lever for improving the levels of schooling among youth.
For example, suppose that teen drinking actually did have an independent
effect on attainment and that every state were to lower their MLDA to
18. The estimates presented here suggest that heavy drinking among high
school seniors would rise by 3.2 percentage points. Since twelfth graders
who drink heavily are at most 8.8 percentage points less likely to enter
college, an MLDA of 18 would only reduce the likelihood of entering
college by 0.28 percentage points ( ). Other policy interven-.032 # .088
tions with larger and more direct links to the schooling decisions made
by teens should be able to promote a greater improvement in the accumulation
of human capital.
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