Are There Civic Returns to Education

Abstract

The hypothesized effects of educational attainment on adult civic engagement and attitudes provide some of the most important justifications for government intervention in the market for education. In this study, I present evidence on whether these externalities exist. I assess and implement two strategies for identifying the effects of educational attainment. One is based on the availability of junior and community colleges; the other, on changes in teen exposure to child labor laws. The results suggest that educational attainment has large and statistically significant effects on subsequent voter participation and support for free speech. I also find that additional schooling appears to increase the quality of civic knowledge as measured by the frequency of newspaper readership.

Full text

Are there civic returns to education?
Thomas S. Dee*
Department of Economics, Swarthmore College, Swarthmore, PA 19081, USA
NBER, USA
Received 30 April 2003; received in revised form 3 November 2003; accepted 8 November 2003
Abstract
The hypothesized effects of educational attainment on adult civic engagement and attitudes
provide some of the most important justifications for government intervention in the market for
education. In this study, I present evidence on whether these externalities exist. I assess and
implement two strategies for identifying the effects of educational attainment. One is based on the
availability of junior and community colleges; the other, on changes in teen exposure to child labor
laws. The results suggest that educational attainment has large and statistically significant effects on
subsequent voter participation and support for free speech. I also find that additional schooling
appears to increase the quality of civic knowledge as measured by the frequency of newspaper
readership.
D2004 Elsevier B.V. All rights reserved.
JEL classification: I2; H4; H23
Keywords: Voting; Civic engagement; Education; Externalities
‘‘... since the achievement of American Independence, the universal and ever-repeated
argument in favor of Free Schools has been, that the general intelligence which they are
capable of diffusing, and which can be imparted by no other human instrumentality, is
indispensable to a republican form of government.’’ Mann (1957)
0047-2727/$ - see front matter D2004 Elsevier B.V. All rights reserved.
doi:10.1016/j.jpubeco.2003.11.002
* Tel.: +1-610-690-5767; fax: +1-610-328-7352.
E-mail address: dee@swarthmore.edu (T.S. Dee).
www.elsevier.com/locate/econbase
Journal of Public Economics 88 (2004) 1697 – 1720

1. Introduction
Economists typically justify the government’s extensive and varied involvement in
the market for education by appealing to distributional concerns and several types of
market failures. The most frequently discussed types of market failure involve the
positive externalities that might be associated with schooling. For example, some have
argued that education generates external social benefits by reducing the prevalence of
crime and by promoting knowledge spillovers and technology diffusion in the
workplace.
1
However, the externality that is arguably featured most prominently in
discussions about education involves civic behaviors and attitudes. Specifically, it is
widely believed that education is an essential component of a stable democratic
society because it encourages citizens to participate in democratic processes and
prepares them to do so in an informed and intelligent manner. The putative existence
of such civic returns to education motivated the proliferation of common schools in
the early 19th century and early educational reformers like Horace Mann and
continues to provide one of the most important justifications for the many public
policies and institutions that promote access to all levels of education.
An extensive, empirical literature in political science has documented a strong
correlation between educational attainment and various civic behaviors. In particular,
this literature has demonstrated that higher levels of schooling are associated with
substantive increases in voter turnout. Political scientists generally interpret this
literature as providing strong support for the view that education is effective at
promoting the quantity and quality of civic participation. However, these correlations
could actually be quite misleading since both schooling and civic outcomes are
simultaneously influenced by a wide variety of inherently unobservable traits specific
to individuals and the families and communities in which they were reared. For
example, individuals who grew up in cohesive families and communities that stressed
civic responsibility may also be more likely to remain in school. The plausible
existence of such unobservables implies that conventionally estimated correlations may
spuriously overstate the true civic returns to education.
2
This study attempts to construct less ambiguous empirical evidence on this policy-
relevant issue by identifying the causal effects of additional schooling on civic
behaviors and knowledge. The research designs adopted here essentially parallel the
extensive, empirical literature on the labor-market returns to schooling (e.g., Angrist
1
See Wolfe and Haveman (2001) for a discussion of the nonmarket and social benefits possibly associated
with education. Poterba (1996) and Taylor (1999) discuss the case for governmental intervention in the market for
education and conclude that there is surprisingly little empirical evidence to indicate whether or not hypothesized,
positive externalities exist. However, several recent empirical studies have assessed the effects of schooling on
knowledge spillovers (e.g., Moretti, in press; Acemoglu and Angrist, 2000) and on criminal behavior (Lochner
and Moretti, 2001; Witte, 1997).
2
An additional concern is that the existence of measurement error in self-reported schooling could lead
correlations to understate the true effects of schooling (Angrist and Krueger, 1999; Card, 1999). The direction of
omitted variable biases could also be negative. For example, the high-ability individuals who continue their
schooling may have higher opportunity costs and may think that voting is largely an expressive act that is
extremely unlikely to actually influence policy.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201698

and Krueger, 1999; Card, 1999). More specifically, these inferences rely critically on
instrumental variables that generated possibly exogenous variation in individual levels
of schooling but that should otherwise be unrelated to adult civic outcomes.
3
First,
using data from the High School and Beyond (HS&B) longitudinal study, I estimate
the effects of college entrance on adult voter and volunteer participation by relying on
the geographic proximity and density of junior and community colleges as a teen.
Then, using data from the 1972–2000 General Social Surveys (GSS), I estimate the
effects of years of schooling on adult voter participation, on group memberships and
on attitudes towards free speech by relying on changes in teen exposure to child labor
laws (Acemoglu and Angrist, 2000). Using the GSS data, I also estimate the effects of
additional schooling on the frequency of newspaper readership, an outcome that is
closely related to measures of civic awareness. The results of these evaluations suggest
that additional schooling, both at the secondary and post-secondary levels, had large
and statistically significant effects on voter participation. I also find that the additional
secondary schooling significantly increased the frequency of newspaper readership as
well as the amount of support for allowing most forms of possibly controversial free
speech.
2. Education and civic engagement
One of the fundamental mechanisms by which education has long been thought to
generate civic externalities involves improvements in the quality of civic participation
and awareness. Specifically, it is widely alleged that increases in education generate
broad social benefits by allowing citizens to make more informed evaluations of the
complex, social, political and technological issues that might be embedded in
campaign literature, legislative initiatives and ballot referenda. However, the contem-
porary literature among political scientists has also put a particular stress on the
positive effects that schooling may have on the likelihood of civic participation, in
particular, voter turnout (e.g., Wolfinger and Rosenstone, 1980). Education could
promote civic participation through at least two broad channels. First, schooling may
reduce the effective costs of certain forms of civic participation. In particular, this is
thought to occur because increased cognitive ability makes it easier to process
complex political information, to make decisions and to circumvent the various
bureaucratic and technological impediments to civic participation.
4
Second, education
may increase the perceived benefits of civic engagement by promoting ‘‘democratic
enlightenment’’ or, stated differently, by shaping individual preferences for civic
activity. Similarly, it is often alleged that education plays an important public role
3
I discuss a variety of ad hoc empirical evidence that is consistent with the maintained assumptions
regarding instrument validity.
4
However, there are other indirect mechanisms by which education may currently lower the effective costs
of voting. For example, since 13 states currently prohibit ex-felons from voting, education may also reduce the
effective costs of voting through its effects on criminal activity. Similarly, to the extent that education increases
the likelihood of having a driver’s license, the recent expansion of ‘‘motor-voter’’ policies may have added to the
effects of education on voter turnout.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1699

by directly inculcating students with other fundamental democratic and pluralistic
values (e.g., support for free speech, for the separation of church and state, etc.).
5
However, it is also possible that additional schooling shapes civic preferences
indirectly through altering the composition of peer groups and shared social norms.
Interestingly, an economic perspective could also suggest alternative mechanisms by
which additional schooling might actually reduce civic engagement. For example, by
raising the opportunity cost of an individual’s time, increased schooling could reduce the
amount of time and attention allocated to civic activity. This could be particularly relevant
for volunteering, which, unlike voting, can involve a substantial commitment of time.
However, education could also reduce voter participation by promoting an awareness of
voting as an essentially expressive act with an infinitesimally small probability of
influencing actual policy.
6
Nonetheless, the available empirical evidence seems to provide
an emphatic confirmation of the conventional view that education does promote civic
engagement. Numerous studies over the last 50 years have demonstrated that higher levels
of individual schooling are strongly associated with civic behaviors and knowledge.
7
For
example, in a widely repeated interpretation of this empirical evidence, Converse (1972)
refers to educational attainment as the ‘‘universal solvent’’ of political participation.
Similarly, Putnam (2001) notes that ‘‘education is by far the strongest correlate that I have
discovered of civic engagement in all its forms’’ (emphasis mine). Also, in their earlier
study of voting participation, Wolfinger and Rosenstone (1980) suggest that their core
finding is the ‘‘transcendent importance of education’’. However, they also note that an
individual’s level of schooling could easily proxy for unobserved traits that also influence
civic behaviors (pp. 19 –20). For example, they suggest that the types of family back-
grounds that promote increased schooling may also promote increased socialization into
civic activities like voting. Wolfinger and Rosenstone (1980), like other researchers in this
field, have attempted to control for the possible bias in the estimated effect of education by
introducing a few additional control variables (e.g., income and occupational measures)
into multiple regression models. The apparent robustness of the correlations between
education and civic outcomes has led most researchers to conclude that education does
have a causal effect. For example, in the most recent contribution to this literature, Nie and
Hillygus (2001) note that this orthodox view is ‘‘largely uncontested’’.
However, the basic approach of introducing a few additional controls may not
convincingly resolve the question of whether the strong correlations between
education and civic outcomes actually reflect the true causal effects. In particular,
this could occur because so many of the shared determinants of civic behavior and
educational attainment are inherently difficult for researchers to measure well. For
example, as noted earlier, children who were raised in families or communities that
5
The preference-shaping nature of schooling is typically viewed as normatively desirable. However, Lott
(1990, 1999) argues that governments use the indoctrination that occurs in pubic schools to support totalitarian
regimes and large wealth transfers.
6
See Mueller (1989) for a discussion of the paradox of voting, models of voting behavior and issues related
to the quality of the vote.
7
See Nie et al. (1996, p. 3) for extensive references to this empirical literature. Educational attainment also
appears to be strongly correlated with civic participation in other countries (e.g., Franklin, 1996).
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201700

stressed civic responsibility are almost certainly more likely to remain in school
longer. This may occur in part because such families and communities are also
likely to impart values that encourage schooling. However, it could also occur
simply because civic-minded families and communities may do more to insure that
their children attend well-funded, high-quality schools. These plausible scenarios
imply that the strong association between adult civic outcomes and educational
attainment may reflect, to an unknown degree, the confounding influence of
unobserved family and community traits. Alternatively, these correlations could also
reflect the confounding influence of other, inherently unobservable individual traits
like the rate at which future outcomes are valued and the taste for altruism.
Certainly, the recent trends in the United States (i.e., increases in educational
attainment not matched by increases in voter turnout or political knowledge;
Galston, 2001) suggest that the association between education and civic engagement
could be specious. And at least two studies in the political science literature provide
more formal evidence that such concerns about omitted variable biases may be
empirically relevant. Both Luskin (1990) and Cassel and Lo (1997) present evidence
that the apparent influence of education on civic outcomes (political literacy and
sophistication) may reflect the spurious influence of other individual traits (e.g.,
intelligence and parents’ socioeconomic status). Similarly, Gibson (2001) presents
within-twin estimates, which suggest that education actually reduces the probability
of volunteering. In the next two sections, I present new empirical evidence on the
effects of educational attainment on several civic outcomes. I attempt to identify the
causal effects of educational attainment by relying on instrumental variables that
generate plausibly exogenous changes in the levels of individual schooling.
8
3. College attendance and civic participation
3.1. High school and beyond (HS&B)
The data for this section are drawn from High School and Beyond (HS&B), a
major longitudinal study conducted by the U.S. Department of Education. This
detailed study began with a cohort of high school sophomores in 1980. Follow-up
interviews of roughly 12,000 members of the sophomore cohort occurred in 1984
when most respondents were 20 years old and again in 1992 when most
respondents were 28 years old.
9
In the 1992 interview, respondents were asked
four civic-related questions: whether they were currently registered to vote
(mean = 0.67), whether they had voted in a local, state or national election within
the past year (mean = 0.36), whether they had voted in the 1988 Presidential election
(mean = 0.55) and whether they had volunteered in the last month (mean = 0.37).
There is evidence that survey respondents, particularly those with more education,
8
A recent study by Milligan et al. (2003) applies a similar methodology to different data sets and finds
results similar to those presented here.
9
See the data appendix in Dee (2003b) for further information on the study and the extract used here.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1701

sometimes overstate their civic participation (e.g., Silver et al., 1986; Bernstein et
al., 2002). However, this does not appear to be a problem with respect to the
HS&B data.
10
The key measure of educational attainment examined here is college
entrance defined as of the 1984 interview (mean =0.54). This definition of college
entrance is based on attendance at a junior college, a community college or a 4-
year college or university and explicitly excludes those who only attended a
vocational, trade, business or other training school. While this is a somewhat
narrow margin of educational attainment, the available evidence indicates that it is
also an increasingly important one. The rate of college enrollment among young
adults has increased dramatically over the last 20 years with roughly half of this
increase being absorbed by junior and community colleges (Kane and Rouse, 1999).
And prior studies suggest that modest persistence at 2 and 4-year colleges has
beneficial labor-market consequences even when it does not result in a degree (e.g.,
Kane and Rouse, 1995). The HS&B respondents who had entered college by 1984
did generally remain in college long enough to accumulate a relatively large amount
of undergraduate credits.
11
Furthermore, the baseline evidence discussed below
demonstrates that this measure of college entrance has a strong partial correlation
with the probability of subsequent civic engagement. However, the choice of college
entrance as a measure of educational attainment is also dictated by the availability
of a plausible instrument, the geographic availability of junior and community
colleges as a teen, which appears to have substantively influenced the decision to
attend college and to have been otherwise unrelated to civic engagement as an
adult.
12
3.2. Baseline estimates
The validity of the geographic availability of junior and community colleges
(hereafter referred to as 2-year colleges) as a basis for identification is a critical
issue and is discussed in some detail below. However, before turning to an
assessment of the relevant instrumental variables, it is useful to establish an
empirical baseline by estimating the effects of college entrance on subsequent civic
10
Specifically, these means are generally comparable to those from contemporaneous Current Population
Surveys (CPS). And, more important, the education gradients for these data are similar or smaller than those
based on CPS and actual voter turnout data (see Dee, 2003b for details). It should also be noted that the potential
existence of reporting bias that is increasing in education would imply that schooling actually had some of its
intended civic consequences.
11
Specifically, data from the HS&B transcript study indicate that those who had entered college by 1984
had, on average, about 80 more semester hours of undergraduate credit than those who did not: the equivalent of
roughly five full-time college semesters. However, a caveat is appropriate since transcript data are missing or
incomplete for roughly 25% of the respondents in this extract.
12
Similarly, I chose to define college entrance as of the 1984 interview when most respondents were 20
years old and not as of later interviews. The estimated effects of college entrance are similar regardless of which
interview is used to define it. However, college entrance defined as of later interviews had a plausibly weaker
relationship to one of the early measures of college availability (i.e., the distance in miles from the high school to
the nearest 2-year college).
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201702

behaviors in specifications that assume the absence of omitted variable biases. Table
1presents the estimated marginal effects from single-equation probits in which the
four measures of civic behavior are the dependent variables. The first specification
(column (1)) conditions on 10 variables representing basic demographic information
on age, race, ethnicity, gender and religious affiliation, 18 other variables that reflect
family income, family composition and parental education as defined during the
1980 interview and a single variable reflecting each respondent’s 1980 composite
score on reading, mathematics and vocabulary tests.
13
The subsequent models
introduce school-level controls (i.e., miles to the nearest 4-year college and urban-
icity fixed effects), state and county-level controls based on the location of the
base-year school, fixed effects for the Census division of the base-year school and,
finally, fixed effects for each of the 961 base-year schools. One of the county-level
variables is a well-measured proxy for the civic attitudes of the community in
which the respondents grew up: the county-level voter turnout in the 1980
Presidential election. The second county-level variable is a measure of adult
educational attainment in the respondent’s teen community: the percent of adults
aged 25 or older with high school degree. The third county-level control, the
population share aged 18–24, may be a relevant determinant of civic engagement
and also influence the competitiveness of post-secondary institutions. The two state-
level variables reflect influential voter regulations defined as of 1992 (Knack, 1995).
One is a binary indicator for whether the state had an active policy of allowing
voter registration by mail. The second is the number of years the state had active
13
See the appendix in Dee (2003b) for details on these controls. The Huber – White standard errors are
adjusted for clustering at the school level.
Table 1
Estimated marginal effects of college entrance on adult civic behaviors, HS&B
Dependent variable Single-equation probit OLS Sample
(1) (2) (3) (4) (5) size
Registered to vote 0.119
(0.011)
0.119
(0.011)
0.122
(0.011)
0.119
(0.011)
0.111
(0.012)
11,366
Voted in last 12 months 0.092
(0.011)
0.092
(0.011)
0.095
(0.011)
0.093
(0.011)
0.080
(0.012)
11,429
Voted in 1988
Presidential election
0.157
(0.012)
0.156
(0.012)
0.160
(0.012)
0.158
(0.012)
0.142
(0.013)
11,370
Volunteered in last
12 months
0.055
(0.010)
0.057
(0.011)
0.056
(0.011)
0.056
(0.011)
0.055
(0.011)
11,484
School-level controls no yes yes yes no
State/county-level controls no no yes yes no
Census division dummies no no no yes no
School fixed effects no no no no yes
All models include binary indicators for gender (1), age (1), race/ethnicity (3), religious affiliation (5), family
income (8), parental education (4) and family composition (5) and the base-year composite test score. Standard
errors, adjusted for clustering at the school level, are reported in parentheses. All the point estimates are
statistically significant at the 1-percent level.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1703

‘‘motor-voter’’ regulations in place.
14
The available evidence suggests that a years-
based measure is the appropriate variable for identifying the early effects of ‘‘motor-
voter’’ policies because state drivers licenses are renewed in cycles as long as 6
years (Knack, 1995).
These models are somewhat unusual in comparison to the prior literature since they
condition on detailed individual and community-level socioeconomic variables defined
as of each respondent’s teen years. Furthermore, HS&B’s clustered sampling design
also makes it possible to control for the possibly confounding influence of unobserved
community traits through the introduction of school fixed effects. The key results from
these evaluations, which are presented in Table 1, uniformly suggest that college
entrance had positive and statistically significant effects on civic participation.
Interestingly, the magnitudes of these estimated marginal effects are also quite robust
to the introduction of the additional controls, including school fixed effects. These
estimated effects are also quite large, suggesting that college attendance has a sizable
influence on subsequent civic participation. For example, these estimates imply that
college entrance increased voter registration by approximately 12 percentage points, an
increase of nearly 18% in the mean probability of being registered. Similarly, these
estimates imply that college entrance increases the mean probability of voting in the
last year, voting in the 1988 Presidential election and volunteering by 26%, 28% and
15%, respectively.
However, the central concern with the results in Table 1 is that the strong partial
correlations between college entrance and civic behaviors may reflect the confounding
influence of unobserved determinants of both schooling and civic engagement. One
straightforward way to assess the possible empirical relevance of this concern is to
examine the partial correlations between college entrance and measures of civic
attitudes and knowledge that preceded attendance in college. I rely on two such
measures based on data from the sophomore-year survey. One is a standardized test
score on questions related to civics. The other is the student’s response to a question
about the importance of correcting social and economic inequality (1 = not important,
2 = somewhat important and 3 = very important). Each of these variables is highly
predictive of each measure of future civic engagement. For example, a 10% increase
in the sophomore-year civics test score is associated with a statistically significant 7%
increase in the mean probability of voting within the last year. Similarly, a one-unit
increase in the ordered attitudinal measure is associated with a statistically significant
10% increase in the mean probability of voting. In auxiliary regressions where these
sophomore-year measures are the dependent variables, the estimated effects of college
entrance are positive and statistically significant. However, since the dependent
variables in these models preceded college entrance, these results cannot plausibly
reflect causal effects. Instead, these results suggest the existence of individual-level
unobservables that may have a positive covariance with both educational attainment
14
‘‘Motor-voter’’ regulations bundle an application for voter registration with those for driver licenses. All
states were required to institute ‘‘motor-voter’’ policies by 1995 as part of the National Voter Registration Act. It
should also be noted that North Dakota does not have voter registration. The results reported here are robust to
excluding observations from respondents who attended high school in that state.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201704

and adult civic engagement. This stylized evidence underscores the need to rely on
instrumental variables in estimating the effects of college attendance on civic
outcomes.
3.3. Measures of college availability as instruments
The partial correlations reported in Table 1 are consistent with the prior empirical
studies of civic participation. However, a more convincing strategy for assessing whether
the estimates in Table 1 reflect the causal effects of attending college is to exploit
instrumental variables that generate plausibly exogenous variation in this measure of
educational attainment. The fundamental requirements of such instrument are that they
actually influence educational attainment and that they are uncorrelated with the unob-
served determinants of civic engagement. A recent study of the labor-market returns to
schooling by Card (1995) suggests that the geographic availability of colleges may provide
valid instruments for schooling.
15
The basic motivation for such instruments is that the
proximity of colleges as a teen should substantially reduce the costs of attending college
(particularly for students from disadvantaged backgrounds) but should otherwise have no
effects on adult outcomes. Rouse (1995) also presents evidence that the availability of 2-
year colleges increases educational attainment for those on the margin of attending college
(a ‘‘democratization’’ effect) but actually reduces it among those who would have
otherwise attended a 4-year college (a ‘‘diversion’’ effect). I also find some support for
a modest ‘‘diversion’’ effect (i.e., the proximity of 2-year colleges reducing the probability
of completing a bachelor’s degree) but rely on the stronger ‘‘democratization’’ effect as a
source of identifying information.
Specifically, I rely on two measures of the local availability of 2-year colleges. One is
the distance in miles from each respondent’s high school to the nearest 2-year college (as
reported by a high-school official as part of the HS&B school survey). The second is a
count of the number of 2-year colleges within each respondent’s county in 1983
(mean = 2.4).
16
These measures of the availability of 2-year colleges are clearly related
but they also appear to have had plausibly distinct effects on educational attainment.
17
For
example, inferences based on these data suggest that the proximity of base-year high
schools to a 2-year college increased college attendance in the late teens and early twenties
had no effect on later spells of college attendance and, overall, may have diverted students
away from eventually completing a bachelor’s degree. In contrast, the number of 2-year
colleges within a county appears to have generated more sustained spells of college
attendance throughout young adulthood and to have increased the probability of ultimately
completing a bachelor’s degree.
15
See Kling (2001) and Currie and Moretti (2002) for further discussions and applications of this approach.
16
These counts were created using the 1983–1984 data from the Higher Education General Information
Survey (HEGIS). See the appendix in Dee (2003b) for details. Card (1995) and Kling (2001) rely similarly on a
binary indicator for any college in county. I also constructed counts of 4-year colleges by county but found that
this was highly collinear with the number of 2-year colleges and exclude it from this analysis. So, a caveat about
attributing the effects associated with this measure to 2-year, not 4-year, institutions is appropriate.
17
These measures are not highly collinear and have a relatively low correlation coefficient of 0.2.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1705

Since the identification strategy implemented here exploits the cross-sectional variation
in the availability of 2-year colleges, the key sources of this variation should be noted.
While every state has 2-year colleges, their geographic distribution across the United
States is somewhat uneven. For example, several states in the West and Southwest (e.g.,
California, Washington, Texas and Arizona) and in the upper Midwest (e.g., Illinois,
Michigan) have relatively extensive systems of public community colleges. The sources of
this variation appear to be independent of the outcomes under study here. Specifically,
Medsker and Tillery (1971) note that this distribution largely reflects the dramatic growth
in new 2-year colleges that occurred in the middle of the last century (i.e., in the decades
prior to the HS&B study). They also state that this growth was shaped by the interaction of
state-specific enabling legislation and several sources of enrollment pressure (e.g., the G.I.
Bill, the baby boom and population migration). However, it should be noted that the states
of New York, Pennsylvania, Ohio and Florida also have a large number of 2-year colleges,
with a particularly large share of them being older, private junior colleges.
I also considered, but rejected, the idea of using proximity to 4-year colleges as an
instrument. Specifically, a central concern with any instrument based on the geographic
availability of colleges is that it might be flawed because it is associated with the
unobserved determinants of both educational attainment and civic behavior. In particular,
the unobserved traits of communities near colleges (e.g., high socioeconomic status) could
simultaneously encourage both higher educational attainment and increased civic partic-
ipation. Furthermore, the availability of colleges may promote a youth-oriented and
politically aware culture that promotes the civic engagement of teens independently of its
effects on educational attainment.
18
I assess the empirical relevance of these concerns by
providing three types of ad hoc empirical evidence on the validity of these instruments.
First, I assess how the effects of these instruments vary across students from advantaged
and disadvantaged backgrounds. To the extent that the estimated effects of these instru-
ments only reflect variation in the costs of attending college, these effects should be
concentrated among students from disadvantaged backgrounds (Card, 1995; Kling, 2001).
Second, I examine their effects on different levels of educational attainment and base-year
test scores. If the estimated effects of college availability truly reflect the costs of attending
college and not the influence of omitted variables, these instruments are likely to have little
or no effects on these other measures of educational achievement.
19
And, third, I examine
the partial correlations between the instruments and sophomore-year measures of civic
attitudes and knowledge that are strongly correlated with future civic participation (i.e.,
scores on a civics test and attitudes towards correcting inequality). The results of all of
these ad hoc specification checks suggest that the proximity to 4-year colleges may be an
18
Another potential complication is that college availability may influence adult civic participation by
raising the educational attainment of community peers. Fortunately, these sorts of spillover effects (e.g., Lochner
and Moretti, 2001) do not appear to be empirically relevant. Specifically, I aggregated the HS&B data to the
county-level and evaluated the reduced-form effects of the instruments on civic participation. The results were
similar to those based on the individual data, which suggests that the spillover effects are empirically negligible.
19
However, a signaling model of education suggests that there could be effects on other levels of attainment
(e.g., Lang and Kropp, 1986). Also, as noted earlier, these instruments could influence higher levels of attainment
through diversion effects (Rouse, 1995).
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201706

invalid instrument. In particular, nearness to 4-year colleges is associated with sharp
increases in the probability of graduating from high school as well as significant increases
in sophomore-year civics knowledge. These results do not constitute a definitive case
against this particular measure as an instrument for educational attainment. Nonetheless,
all of the models for educational attainment and civic outcomes reported here condition on
this measure.
20
In Table 2, I present the key results of these evaluations with respect to the preferred
instrumental variables. The results in the top right panel indicate that both measures of 2-
year college availability have plausibly signed and statistically significant effects on
college entrance. Specifically, these indicate that a location 100 miles further away from a
2-year college reduces the probability of college entrance by 7.3 percentage points.
Similarly, these results suggest that an additional 2-year institution within county is
associated with a 0.6 percentage point increase in the probability of entering college.
21
In
the bottom panel of Table 2, I provide some ad hoc evidence on the validity of these
instruments by estimating their unique effects on students from advantaged and disad-
vantaged backgrounds. Card (1995) suggests that, if the interpretation of college
availability as an independent measure of the costs of attending college is a valid one,
the effects of these instruments should be concentrated among students from disadvan-
taged backgrounds. Following Card (1995), I assess the existence of such response
heterogeneity by interacting the availability measures with indicators for high and low
parental education.
22
The results indicate that the effects of the availability of 2-year
colleges on college entrance are highly concentrated among students with poorly educated
parents.
The results presented in Table 2 also indicate that these instruments are plausibly
related to other measures of educational achievement. Specifically, these estimates
indicate that the availability of 2-year colleges had small and statistically insignificant
effects on base-year composite test scores, on the probability of graduating from high
school and on the probability of obtaining an associate’s degree. These results also
suggest that the geographic proximity of 2-year colleges led to relatively small and
weakly significant reductions in the probability of obtaining a bachelor’s degree: a
‘‘diversion’’ effect that appears to be concentrated among students from disadvantaged
backgrounds. However, the results in Table 2 also suggest that, particularly for
students with poorly educated parents, the number of 2-year colleges within the
county had strong ‘‘democratization’’ effects that increased the probability of entering
20
Not surprisingly, models that use this measure as an IV return estimates somewhat larger than those
reported here.
21
These models condition on all the individual, family, school, county and state-level controls and division
fixed effects. Specifications that incrementally introduce these controls generate similar results (Dee, 2003b).
Since recent studies (Bound et al., 1995; Staiger and Stock, 1997) have illustrated the biases that might be
generated by relying on relatively ‘‘weak’’ instruments, I also tested the joint significance of these two variables.
The extremely low p-values associated with these tests suggest that those concerns are not relevant in this
application (Dee, 2003b).
22
As in Card (1995), low parental education implies that the highest educational attainment of the parents is
high school dropout or missing. Students for whom parents’ education is missing have lower levels of attainment
than the students who report their parents are dropouts.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1707

college as well as the probability of obtaining a bachelor’s degree.
23
But the more
general and important result from these comparative models is that the effects
associated with the availability of 2-year colleges are highly concentrated on the
margin of attending college. This evidence is consistent with the maintained assump-
tion that these measures reflect plausibly exogenous variation in the costs of college
entrance and not other unobserved traits of these communities. In particular, because
these instruments have such large and narrowly focused effects on this single margin
23
As noted earlier, these results for attaining a bachelor’s degree are consistent since the proximity of a
single institution may promote diversion while the availability of several could facilitate the ultimate progression
to a bachelor’s degree.
Table 2
Estimated marginal effects of college availability on base-year variables and educational attainment, HS&B
Independent variable Base-year variables Educational attainment
Civics test Inequality
attitude
Composite
test
High school
graduate
College
entrant
Associate’s
degree
Bachelor’s
degree
Model (1)
Miles to a 2-year
college (H100)
0.250
(0.417)
0.021
(0.029)
0.83
(2.0)
0.003
(0.012)
0.073
z
(0.025)
0.018
(0.020)
0.032*
(0.019)
Number of 2-year
colleges in county
0.005
(0.023)
0.002
(0.002)
0.07
(0.10)
0.0004
(0.001)
0.006
z
(0.002)
0.002
(0.002)
0.003
y
(0.0019)
Model (2)
Low parental
education miles
to a 2-year college
(H100)
0.046
(0.438)
0.045
(0.039)
1.09
(1.9)
0.004
(0.014)
0.133
z
(0.035)
0.015
(0.031)
0.049*
(0.025)
High parental
education miles
to a 2-year college
(H100)
0.421
(0.562)
0.001
(0.041)
0.61
(2.5)
0.011
(0.014)
0.028
(0.034)
0.021
(0.023)
0.022
(0.024)
Low parental
education number
of 2-year colleges
in county
0.012
(0.032)
0.001
(0.003)
0.06
(0.11)
0.0004
(0.001)
0.008
z
(0.002)
0.002
(0.002)
0.006
z
(0.002)
High parental
education number
of 2-year colleges
in county
0.016
(0.027)
0.003
(0.002)
0.17
(0.13)
0.0004
(0.001)
0.005
y
(0.002)
0.002
(0.002)
0.002
(0.002)
Sample size 9751 10,336 11,489 11,475 11,489 11,343 11,343
All models include binary indicators for gender (1), age (1), race/ethnicity (3), religious affiliation (5), family
income (8), parental education (4) and family composition (5), school-level controls (3), state/county-level
controls (5) and Census division dummies (8). The first three models were estimated by OLS; the remaining
results are based on single-equation probits and include base-year composite test scores as a control. Standard
errors, adjusted for clustering at the school level, are reported in parentheses.
* Statistically significant at the 10% level.
y
Statistically significant at the 5% level.
z
Statistically significant at the 1% level.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201708

of educational attainment, it suggests that they do not proxy for the unobserved
determinants of future civic engagement.
Table 2 contains additional evidence on the validity of these exclusion restrictions
based on two sophomore-year variables that reflect each student’s latent civic
engagement and knowledge: a standardized test score on questions related to civics
and an attitudinal question about the importance of correcting social and economic
inequality (1 = not important, 2 = somewhat important and 3 = very important). These
variables, which are highly predictive of future civic participation as an adult, provide
a potentially plausible basis for evaluating the validity of the instruments. Specifically,
if the measures of college availability have an association with the unobserved
determinants of future civic engagement, we would expect them to be correlated with
these observed measures as well. However, the regression results in Table 2 uniformly
indicate that the availability of 2-year colleges, both generally and for students with
poorly educated parents, has a small and statistically insignificant association with
sophomore-year civics knowledge and with attitudes towards inequality.
3.4. Results
The results summarized in Table 2 are consistent with the maintained assumption
that the geographic availability of 2-year colleges provides a potentially valid source
of identification. The availability of 2-year colleges is associated with a significant
increase in college attendance but smaller and statistically insignificant changes in
base-year test scores and in other measures of educational attainment. These increases
are plausibly concentrated among students with poorly educated parents. And these
measures are unrelated to sophomore-year indicators of civic attitudes (e.g., civics
knowledge and attitudes towards inequality). In Table 3, I present the key results from
bivariate probits in which the adult civic behaviors are the dependent variable of
interest and college entrance is an endogenous regressor (Wooldridge, 2002).
24
The
excluded instruments are miles to the nearest 2-year college and the number of 2-year
colleges within county. These results of these models suggest that college entrance has
relatively small (but imprecisely estimated) effects on the probability of volunteering.
However, the estimated effects of college entrance on each of the three measures of
voter participation are uniformly large and positive. Specifically, these estimates
indicate that college entrance increases voter participation by roughly 17 to 22
percentage points.
These results are clearly consistent with the conventional claims that educational
attainment is a critical determinant of civic engagement. In fact, with respect to voter
24
The estimates from 2SLS models are similarly signed and statistically significant estimates but are
substantially larger than the marginal effects and average treatment effects (ATE) based on these bivariate probits,
particularly in models saturated with the additional controls. This raises the critical issue of whether identification
in the bivariate probits relies on possibly unjustified assumptions about functional form, instead of the exclusion
restrictions. The available evidence suggests that this is not the case. Specifically, I found that bivariate probits
that do not include the instrumental variables lead to smaller and statistically insignificant effects. Altonji et al.
(2002, appendix) discuss similar issues in the context of the literature on the effects of Catholic schooling.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1709

registration and having voted in the last 12 months, these estimated effects are
noticeably larger than those based on partial correlations (Table 1). However, the
sampling variation associated with these estimates clearly suggests that these differ-
ences should not be overemphasized. In particular, the hypothesis that the error terms
for college entrance and each measure of civic participation are uncorrelated cannot be
rejected in any of the models presented in Table 3. Nonetheless, it is also worth
noting at least three reasons that the true effects of educational attainment on voter
participation might exceed the estimates based on partial correlations (Table 1). First,
as frequently noted in the literature on wages and schooling, this could reflect an
attenuation bias driven by measurement error in reported schooling. Second, these
estimates could indicate that the civic returns associated with college entrance are
particularly large for the nonrandom subset of individuals whose post-secondary
attainments were influenced by the instruments (e.g., those from disadvantaged
backgrounds, Imbens and Angrist, 1994).
25
And, third, a downward bias in conven-
tional estimates could also reflect the influence of unobserved ability on both
schooling decisions and time allocated to civic endeavors.
However, a fourth possibility with very different implications is that the size of
these estimates reflects undiagnosed violations of the maintained exclusion restric-
tions. One indication that this is not so is that the results from Table 3 are quite
similar across models that incrementally introduce the school, county and state-level
controls. However, another way to assess this concern is to use as instruments the
interaction of low parental education and the measures of 2-year college availability.
Specifically, in such models, the interaction of high parental education and the
measures of 2-year college availability can then be included as controls in the
outcome equations (e.g., Card, 1995). This approach to identification can provide
effective controls for the possible, indirect effects on civic outcomes associated with
25
The results from single-equation probits (i.e., as in Table 1) that allow the effect of college entrance to vary
by parental education suggest that the effects of college entrance on voter registration and turnout are larger
among those with poorly educated parents.
Table 3
Estimated effects of college entrance on adult civic behaviors, bivariate probit, HS&B
Dependent variable b
ˆMarginal
effect
ATE Sample
size
Registered to vote 0.607
y
(0.263) 0.218 0.215 11,366
Voted in last 12 months 0.482
y
(0.196) 0.176 0.174 11,429
Voted in 1988 Presidential election 0.453* (0.256) 0.178 0.171 11,370
Volunteered in last 12 months 0.124 (0.213) 0.047 0.045 11,484
All models include binary indicators for gender (1), age (1), race/ethnicity (3), religious affiliation (5), family
income (8), parental education (4) and family composition (5), base-year composite test score, school-level
controls (3), state/county-level controls (5) and Census division dummies (8). The two instrumental variables are
miles to a 2-year college and the number of 2-year colleges in county. Standard errors, adjusted for clustering at
the school level, are reported in parentheses.
* Statistically significant at the 10% level.
y
Statistically significant at the 5% level.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201710

college availability to the extent that these effects are constant across students with
different family backgrounds. The results based on this specification are similar to
those reported in Table 3 (Dee, 2003b). The robustness of these results suggests that
the basic identifying assumptions are accurate. I also assessed this issue by relying
alternatively on miles to a 2-year college and number of 2-year colleges in county as
the sole instrument and including the other variable as a control. This approach leads
to similarly large and positive point estimates in models for voter registration and
turnout. However, in most cases, the reduction in identifying assumptions makes these
estimates statistically imprecise.
4. Secondary schooling and civic outcomes
4.1. General social surveys (GSS)
The evidence from the HS&B data has at least two critical shortcomings. One is
that it only identifies the civic returns to education at the post-secondary level. And
the second is that the available data provide no measures of the degree of civic
awareness or of other fundamental civic values. The data from the General Social
Surveys (GSS) provide an opportunity to address both of these concerns. The GSS is
a nationwide survey, conducted every 1 to 2 years, on a broad range of attitudes and
behavior.
26
My extract is based on the pooled 1972–2000 surveys and consists of the
respondents who lived in the US at age 16 and were 14 years old between 1914 and
1978. In each survey, these respondents were asked about their educational attainment
and whether they voted in the last Presidential election. On average, 73% of the GSS
respondents claimed to have voted in the most recent Presidential election.
27
In most, but not all, survey years, GSS respondents were also asked about how
often they read the newspaper, about their group memberships (e.g., fraternal and
community-service groups, political clubs, school-service and youth groups, church-
service groups, etc.) and about their attitudes towards free speech for particular groups.
The GSS respondents report an average of 1.8 group memberships. The frequency of
newspaper readership is based on five possible responses (never, less than once a
week, once a week, a few times a week and every day) coded here as varying from 0
to 4 (mean = 3.2). This measure of newspaper readership is meant to indicate whether
voters stay informed about current affairs. There are inarguably better ways of
measuring the degree of civic awareness. For example, in 1987, the GSS respondents
were asked to identify their congressional representative. Interestingly, only 37% of
respondents were able to answer this question correctly. Unfortunately, since this
question was only asked in 1987, there are relatively few observations (n= 1555) and
a plausible identification strategy cannot be implemented. However, the data from
26
See the appendix in Dee (2003b) for details on the GSS and construction of this extract.
27
There does not appear to be a propensity for better-educated GSS respondents to overstate their voter
turnout. In particular, the education gradients based on CPS data and on county-level data reflecting actual voter
turnout are similar or larger than those reported in Table 4 (Dee, 2003b).
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1711

1987 do indicate that the frequency of newspaper readership is strongly associated
with being able to identify your congressman. Specifically, conditional on all the
covariates discussed below, a one-unit increase in the measure of newspaper readership
is associated with a 10 percentage-point increase in the probability of answering
correctly (i.e., a 27% increase in the mean). This suggests that the frequency of
newspaper readership is a reasonable proxy for the degree of civic awareness. The
measures of attitudes towards free speech are based on separate survey questions that
allowed respondents to indicate whether they would allow particular types of people to
speak in their community. These types include someone against churches and religion
(an anti-religionist), an admitted Communist, an admitted homosexual, someone who
advocates outlawing elections and letting the military run the country (a militarist) and
someone who believes blacks are inferior (a racist). Support for allowing free speech
ranges from 59% for the militarist to 73% for the homosexual (see Dee, 2003b).
4.2. Baseline estimates
In Table 4, I present baseline OLS estimates of how years of completed schooling
influences these measures of civic engagement and attitudes. The sparsest specification only
includes as controls basic demographic information (9 variables) and fixed effects for survey
year (as many as 22 variables), year of birth (64 variables) and Census division of residence
at age 16 (8 variables). The second specification adds three control variables that reflect the
quality of public schools and the degree of civic engagement in each respondent’s teen
community. The two school quality measures are the pupil– teacher ratios and relative
teacher salaries in public schools at age 14 in the Census division of residence at age 16.
28
The third variable is the voter turnout in the Presidential election that occurred between the
ages of 13 and 16 in the Census division of residence at age 16. The third specification
introduces variables based on survey responses that reflect a variety of family and
community-specific traits. These include family income at age 16 (five variables), family
structure at age 16 (five variables), parental education (four variables) and the urbanicity of
residence at age 16 (six variables). In the final model, I control for all the unobserved
determinants that might be specific to a particular Census division in a particular year (e.g.,
weather, close political races, etc.) by including approximately 200 fixed effects for each
unique Census-division and survey-year combination. The standard errors are adjusted for
unspecified heteroscedasticity specific to the Census division of resident at age 16.
29
The
OLS results in Table 4 uniformly indicate that schooling is strongly and positively correlated
28
Card and Krueger (1992) present evidence that these measures influenced average years of schooling. I
converted average teacher salaries to a relative measure by exploiting data on wages paid to road workers on
Federal projects (Card and Krueger, 1992) and data on wages for production workers in manufacturing. See the
appendix in Dee (2003b) for information on the construction of these variables.
29
This conservative approach may be appropriate since the pre/post nature of the instrumental variable and
serial correlation in the dependent variables could lead to overstated precision (Bertrand et al., 2002).Asa
practical matter, this only appears to increase the 2SLS standard errors slightly. However, this approach is also a
conservative one because the existence of only nine Census divisions implies there are only 8 degrees of freedom
in the critical value of the t-statistics.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201712

with all of these measures of civic engagement and attitudes. For example, these estimates
suggest that an additional year of schooling increases voter participation by 3.8 percentage
points, an increase of approximately 5%. These results also imply that another year of
schooling significantly increases the index of newspaper readership (by 0.104, an increase of
3%) and the number of group memberships (by 0.222, an increase of 12%). Another year of
schooling also appears to increase support for free speech by a statistically significant 2.2 to
3.6 percentage points, depending on who is doing the speaking. Interestingly, these
estimated effects are generally quite robust to dramatic increases in the set of controls for
observed traits.
Table 4
OLS and 2SLS estimates of the effect of highest grade completed on civic behaviors and attitudes, 1972 – 2000
GSS
Dependent (1) (2) (3) (4) Sample
variable OLS 2SLS OLS 2SLS OLS 2SLS OLS 2SLS size
Voted in last
Presidential
election
0.043
z
(0.002)
0.037*
(0.019)
0.038
z
(0.002)
0.064
(0.036)
0.038
z
(0.002)
0.069*
(0.036)
0.038
z
(0.002)
0.068*
(0.035)
32,111
Newspaper
readership
0.112
z
(0.013)
0.203
z
(0.021)
0.104
z
(0.014)
0.127*
(0.066)
0.105
z
(0.014)
0.112*
(0.056)
0.104
z
(0.014)
0.113*
(0.056)
21,805
Group
memberships
0.239
z
(0.009)
0.138
y
(0.047)
0.221
z
(0.011)
0.144
(0.108)
0.222
z
(0.011)
0.157
(0.141)
0.222
z
(0.011)
0.164
(0.184)
16,361
Allow anti-
religionist
to speak
0.036
z
(0.001)
0.092
z
(0.032)
0.030
z
(0.001)
0.137
z
(0.028)
0.030
z
(0.001)
0.126
z
(0.024)
0.029
z
(0.001)
0.125
z
(0.021)
22,449
Allow
communist
to speak
0.043
z
(0.002)
0.060
y
(0.026)
0.036
z
(0.002)
0.085
z
(0.019)
0.036
z
(0.002)
0.084
z
(0.020)
0.036
z
(0.002)
0.080
z
(0.021)
22,111
Allow
homosexual
to speak
0.035
z
(0.002)
0.092
z
(0.018)
0.029
z
(0.001)
0.138
z
(0.026)
0.029
z
(0.001)
0.126
z
(0.021)
0.029
z
(0.001)
0.123
z
(0.028)
20,678
Allow militarist
to speak
0.037
z
(0.002)
0.005
(0.027)
0.031
z
(0.002)
0.054
y
(0.023)
0.030
z
(0.002)
0.053*
(0.025)
0.030
z
(0.002)
0.036
(0.031)
18,514
Allow racist
to speak
0.027
z
(0.002)
0.040
(0.031)
0.023
z
(0.002)
0.022
(0.032)
0.022
z
(0.002)
0.020
(0.031)
0.022
z
(0.002)
0.002
(0.032)
18,488
Teen-division/
cohort
controls
no yes yes yes
Family/
community
controls
no no yes yes
Current-division-
by-survey-
year dummies
no no no yes
All models include age, age squared and binary indicators for gender (1), race (2) and religious preference (4) and
fixed effects for survey year, year of birth and Census division of residence at age 16. Standard errors, adjusted for
clustering at the division level, are reported in parentheses.
* Statistically significant at the 10% level.
y
Statistically significant at the 5% level.
z
Statistically significant at the 1% level.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1713

4.3. Restrictive child labor laws as an instrument
The OLS estimates in Table 4 suggest that additional years of schooling led to
significant increases in the quality and quantity of civic engagement and in the support
for free speech. I attempt to assess whether these estimates reflect a causal relationship by
exploiting the exogenous variation in years of schooling generated by teen exposure to
restrictive child labor laws. Recent studies by Acemoglu and Angrist (2000) and Lleras-
Muney (2002) provide evidence that the variation in child labor laws influenced the
amount of schooling at the secondary level. The coding of the data on child labor laws
used here is discussed in detail in Acemoglu and Angrist (2000). Essentially, for each state
and year from 1914 to 1978, they identified the minimum amount of schooling required
before a child could enter the workforce (the variable CL). This variable is equal to the
greater of the years of schooling a state required before granting a work permit and the
difference between the age at which children could work and the age at which they had to
enter school. These laws are represented here by a dummy variable equal to one for CL
greater than or equal to 9.
30
These state-year laws could not be matched directly to GSS
respondents because the available data only identifies which of nine Census divisions they
resided in at age 16. Therefore, I calculated division-by-year means of these state-year
dummies using state-year population estimates as weights. I then matched each GSS
respondent to these fractional variables representing restrictive child-labor laws that were
in effect at age 14 in their reported division of residence at age 16. This unusual division-
by-year aggregation undoubtedly introduces some measurement error into the instruments.
However, it is not clear that the implied measurement error is any less than that in other
studies, which rely on matches by state of birth, not state of teen residence. Furthermore,
an auxiliary regression indicates that this division-year measure of restrictive child labor
laws captures a substantial proportion of within-state variation in these laws. Specifically, I
regressed a state-year indicator for a CL of 9 or higher on the division-year measure for a
CL of 9 or higher, state fixed effects and year fixed effects. The coefficient on the division-
year measure was 0.72 with a t-statistic of 26.
In Table 5, I present the estimated effects of restrictive child-labor laws on different
levels of educational attainment based on specifications that include the full set of controls
(i.e., as in Model (4) in Table 4). The results indicate that restrictive child-labor laws
increased years of schooling by a statistically significant 0.53 years. This point estimate is
somewhat larger than those reported by Acemoglu and Angrist (2000). Specifically, they
found (Table 4, p. 30) that a CL of 9 or higher increased years of schooling by 0.4 years
among 40–49-year-old white males from the 1950 –1990 Censuses. However, these
differences are small relative to the sampling variation. Furthermore, these modest
differences also appear to reflect the unique composition of the sample analyzed by
Acemoglu and Angrist (2000). The first-stage effects of CL9 are smaller (and more
imprecise) when the GSS sample is similarly limited to prime-age, white males.
30
In some models based on PUMS data, Acemoglu and Angrist (2000) find that CL of 7 and 8 had smaller
but statistically significant effects on years of schooling. Estimates based on the GSS also suggest that CL of 7
and 8 had positive but smaller effects. However, since the GSS has relatively few observations, these effects are
always estimated imprecisely and do not provide a plausible source of identifying information.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201714

The quality of the measure of restrictive child-labor laws as an instrument hinges
critically on the maintained assumption that these estimates accurately reflect its
independent effects on educational attainment. The evidence from prior studies is
generally consistent with this view. For example, Lleras-Muney (2002) presents a
variety of ad hoc empirical evidence on changes in child-labor laws and concludes that
they were not endogenously determined. Furthermore, Goldin (2001) argues that such
laws played a relatively minor role in the dramatic ‘‘high school movement’’ from 1910
to 1940, which suggests that these law changes were not part of substantive social
changes that might have also influenced civic attitudes. The robustness of the first-stage
estimates to the introduction of additional controls also provides some supporting
evidence (Dee, 2003b).
The remaining results in Table 5 also provide indirect evidence on the validity of
these instruments. More specifically, if these models effectively identify the influence
of stricter child-labor laws on educational attainment, we should find that these
estimated effects are largely concentrated at the lower end of the distribution of
educational attainment (Acemoglu and Angrist, 2000; Lleras-Muney, 2002). However,
we should be especially concerned about the existence of undiagnosed specification
errors if similarly specified models indicate that these laws had relatively large effects
on higher levels of educational attainment. The results in Table 5 indicate that the
effects associated with stricter child-labor laws were largely concentrated at the
secondary level. More specifically, these estimates indicate that the strictest child-labor
laws led to large and statistically significant increases in the probability of completing
9, 10, 11 and 12 years of schooling and the probability of high school graduation.
However, the same specifications indicate that these law changes had smaller and
statistically insignificant effects on several measures of post-secondary educational
Table 5
OLS estimates of the effects of restrictive child-labor laws on measures of educational attainment, 1972– 2000
GSS
Dependent variable b
ˆ
Highest grade completed 0.53
z
(0.14)
Completed 9th grade or higher 0.12
z
(0.02)
Completed 10th grade or higher 0.10
z
(0.01)
Completed 11th grade or higher 0.10
z
(0.02)
Completed 12th grade or higher 0.10
z
(0.01)
High school graduate 0.08
z
(0.02)
Completed at least 1 year of college 0.04 (0.03)
Associate’s degree 0.03 (0.02)
Bachelor’s degree 0.03 (0.02)
The sample size is 32,111. All models include age, age squared, binary indicators for gender (1), race (2),
religious preference (4), family income at age 16 (5), parental education (4) and family composition at age 16 (5),
urbanicity of residence at age 16 (6), pupil–teacher ratio at age 14, relative teacher salaries at age 14, voter
turnout as a teen and fixed effects for year of birth, Census division of residence at age 16 and current division-of-
residence by survey-year dummies. Standard errors, adjusted for clustering at the division level, are reported in
parentheses.
z
Statistically significant at the 1% level.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1715

attainment. Another similarly ad hoc way to assess the validity of this identification
strategy is to note that the variation in child-labor laws should be particularly relevant
for respondents who had relatively disadvantaged backgrounds. I examined this
possibility by estimating how the effects of stricter child-labor laws varied across
respondents with low and high levels of parental education.
31
The results indicated that
the increases in educational attainment associated with more restrictive child-labor laws
were larger among those who had more poorly educated parents. Specifically, using the
voting sample, the estimated effect of these laws was 0.75 among those with poorly
educated parents and 0.36 among the remaining respondents. However, it should be
noted that this difference, though suggestively plausible, is not statistically meaningful.
4.4. 2SLS results
The results in Table 5 suggest that restrictive child labor laws provide a valid source of
information for identifying the effects of years of schooling on adult civic behaviors. In
Table 4, I present 2SLS estimates based on this instrument in models for each measure of
civic engagement.
32
The results indicate that schooling has uniformly positive and
statistically significant effects on most measures of civic engagement and attitudes. For
example, these 2SLS estimates suggest that an additional year of schooling increased voter
participation by a weakly significant 6.8 percentage points (t-statistic = 1.93). While this
estimate is nearly twice as large as the OLS estimate, this difference is not particularly
large relative to the sampling variation. More formally, a Hausman test fails to reject the
hypothesis that the corresponding OLS estimate is consistent. Interestingly, the effect sizes
from the voting models are quite similar to those based on post-secondary attainment and
the HS&B data. Specifically, the college entrants in HS&B had roughly 2.5 more years of
schooling than nonentrants and the results in Table 3 suggest that this additional schooling
increased voter turnout by 16 to 17 percentage points. The 2SLS results in Table 4 suggest
that 2.5 years of secondary schooling would also increase voter turnout by roughly 17
percentage points (2.5 0.068).
The 2SLS estimates in Table 4 also suggest that schooling increases the quality of
civic engagement and knowledge. More specifically, the 2SLS estimates imply that an
additional year of schooling generates a weakly significant increase (t-statistic = 2.02) in
the frequency of newspaper readership that is roughly equivalent to that implied by the
OLS estimate. The estimated effect of schooling on group memberships is also positive
but highly imprecise. However, these estimates also imply that that schooling signifi-
cantly increased support for free speech by anti-religionists, communists and homo-
sexuals. These estimated effects (8.0 to 12.5 percentage points) are several times larger
than those implied by the corresponding OLS estimates.
33
In contrast, the estimated
31
Low levels of parental education implied that the highest attainment among the parents was less than a
high school degree or missing.
32
I also experimented with specifications that recognized the categorical nature of the dependent variable
and the potential endogeneity of schooling (Wooldridge, 2002) and found that they generated similar results.
33
Hausman tests indicate that the consistency of the OLS estimates can be rejected with regard to free speech
for anti-religionists and homosexuals but not with respect to free speech for communists.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–17201716

effects of schooling on support for speech by militarists and racists are smaller and
statistically imprecise. One concern that is suggested by the relative size of some of the
2SLS estimates is that they are due to the biases from ‘‘contagion’’ effects (e.g., Lochner
and Moretti, 2001). This refers to the possibility that these 2SLS estimates reflect how
restrictive child labor laws influenced both an individual’s schooling as well as that of
his peers. One simple way to assess the empirical relevance of this issue is to replicate
the 2SLS models after aggregating the data to cells defined by the interaction of birth
year and division of residence at age 16 (n= 585). The 2SLS estimates based on these
aggregate data reflect both individual and contagion effects. I found that the estimated
effects of schooling were quite similar to those in Table 4, suggesting that any contagion
effects were negligible.
34
5. Conclusions
In this study, I presented an empirical analysis of one of the fundamental relation-
ships that motivates public policies towards education: the effects of schooling on civic
participation and attitudes. In particular, I assessed whether increases in educational
attainment have causal effects on civic outcomes by exploiting possibly exogenous
sources of variation in schooling that should otherwise be unrelated to civic outcomes
in adulthood (i.e., the geographic availability of 2-year colleges as a teen and exposure
to child labor laws as a teen). The results suggested that educational attainment, both
at the post-secondary and the secondary levels, has large and independent effects on
most measures of civic engagement and attitudes. The apparent existence of these civic
returns implies that much of the long-lived hyperbole about the important role of
education in a functioning democracy may be accurate. However, it should be noted
that a great deal of the discussion surrounding the role of education in a democracy
has also confused the existence of these externalities with the fundamental issues of
how the government should intervene in the market for education (e.g., price subsidies,
regulation of the private sector, public production). In particular, the existence of large
civic returns to education is not necessarily relevant to the difficult question of
whether government should be involved in directly producing education (i.e., the
‘‘choice of instrument’’ problem, Poterba, 1996). In fact, there is some suggestive
evidence that most private schools are actually more effective than public schools in
promoting civic engagement (e.g., Dee, 2003a; Campbell, 2001). Nonetheless, the
results presented here clearly underscore the dramatic relevance of schooling to the
critical functions of a democratic society and imply that initiatives to promote
educational attainment merit the continued and careful scrutiny of researchers and
policymakers.
34
This is not entirely surprising since over 20% of GSS respondents were not even living in the Census
division in which they resided at age 16.
T.S. Dee / Journal of Public Economics 88 (2004) 1697–1720 1717

Acknowledgements
I would like to thank Cecilia Rouse, William Evans, Orley Ashenfelter, Jon Gruber,
three anonymous referees and seminar participants at Syracuse, Maryland, Princeton,
NBER, Delaware and the National Academy of Education for their helpful comments. I
would also like to thank Josh Angrist for providing data on child labor laws and the
National Academy of Education, the Spencer Foundation and the Center for Information
and Research on Civic Learning and Engagement (CIRCLE) for their financial
assistance. The usual disclaimers apply.
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