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Does College Education Reduce Obesity? Evidence From Vietnam War Draft
Avoidance Using a Regression Discontinuity Analysis1
Bo MacInnis
Abstract
The close tie between the natural age of college attendance and the draft during the
Vietnam war era creates a quasi-natural experiment that encompasses a regression discontinuity
research design. Using the National Health Interview Survey 1998–2003, we exploit this quasi-
natural experiment to study the effect of a specific draft avoidance behavior—enrolling in
college to avoid the draft—on college completion and the effect of college education on obesity
and related health outcomes. The identification condition is that individuals have some, but not
complete, control over their chance of completing college.
In contrast to compulsory school attendance (Angrist and Krueger 1991), we find that
Vietnam war draft avoidance behavior generates a strong instrument for post-secondary
education—causing about a 5% increase in college completion, but has no effect for grades
below high school. Our results support the hypothesis that college education improves physical
health: it reduces the probability of obesity by about 40–60% and obesity co-morbidities such as
hypertension, diabetes, and dental loss by about 30–60%. Robust to a variety of specification
checks, our findings indicate that the traditional return to schooling estimates, that typically only
focus on monetary earnings, greatly underestimate the benefits of schooling.
1 I am grateful to Kenneth Chay for his helpful suggestions that improved the paper. I also thank Jeffrey Perloff, Gordon Rausser, and Elisabeth Sadoulet. Corresponding address: Department of Agriculture and Resource Economics, University of California, Berkeley, CA 94720-3310. E-Mail: [email protected]. All data extracts and programs used in producing the results contained in this paper are available from the author upon request.
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1. Introduction
Education and health are the two most basic forms of human capital stock, and there is a
strong positive relationship between them. Obesity2 is a health outcome with rising economic
importance. In the U.S. today, nearly one-third of adults (over 60 million) and one-sixth of
children (over 9 million) are obese. Obesity increases the risk of heart disease, diabetes, several
types of cancer and other diseases, and contributes to the nation’s health care costs at a growing
rate. Obesity-related medical expenditure was $78.5 billion in 1998, accounting for 9.1 percent
of total annual U.S. medical expenditures (Finkelstein, Fiebelkorn, and Wang 2003). Obese
individuals incur higher health care costs than normal-weight individuals, and the higher
spending is mainly attributable to treatment for diabetes and hypertension (Thorpe, Florance,
Howard, and Joski 2004).
Obesity is associated with low socioeconomic status, but no study has attempted to show
whether education has a causal effect on obesity. Our goal is to fill this important void. The
endogeneity of educational attainment makes it difficult to establish a causal relationship
between education and obesity, or health in general because what makes an individual achieve a
high level of schooling can be correlated with what makes her/him lean. Given the infeasibility
of random assignment of educational attainment, we exploit the Vietnam War draft avoidance
behavior as a quasi-natural experiment to infer causation from education to obesity. During the
peak draft years of the Vietnam war era, the government offered a draft deferment to men
enrolled in college. Some males born between 1946 and 1950 enrolled in and/or remained in
college specifically to obtain this deferment, as the age susceptible to begin drafted correlated
2 Obesity is defined as having a Body Mass Index (BMI) of 30 or more for individuals aged 19 and above; BMI is defined as the ratio of body weight in kilograms to the square of height in meters.
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closely to a natural college age. Consequently, there was a surge in college enrollment
completion rates for these most affected males.
Since it was first documented by Card and Lemieux (2001), several studies (Grimard and
Parent 2005, De Walque 2004) have exploited this quasi-natural experiment to study the causal
effect of education on smoking, where education is instrumented by a measure of induction risk
or being an affected male (typically, males born between 1946 and 1950). The identification
assumption rests on the exclusion restriction: the reason these males enrolled in college to avoid
the draft does not affect their likelihood of smoking or being lean (Angrist, Imbens, and Rubin
1996). However, the exclusion restriction is likely to be violated because individuals self-
selected into college enrollment; this consequently reduces the credibility of the IV estimate to
be interpreted as casual3.
Our contribution is to employ a regression discontinuity design to obtain a causal
estimate under a much weaker identification condition: individuals could have some, but not
complete, control over the fact of their college enrollment (Lee 2005). In a regression
discontinuity design, the probability of treatment status (college enrollment or completion) is
determined by some observed variable that takes a continuum of values, such as whether it
exceeds some known threshold. Identification relies on the existence of a subgroup of individuals
for whom treatment status changes discontinuously at the known threshold, because individuals
close to the threshold are similar in that the mean outcome for those just below the threshold
constitutes the valid counterfactual for those just above the threshold (Hahn, Todd, and van der
Klaauw 2001).
3 For example, what made those affected males complete college—such as having educated and wealthy parents, having established good lifestyles—may also simultaneously reduce their chance of being obese.
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The close tying between the ages of college attendance ages and susceptibility to the draft
creates a discontinuity in the relationship between college education and birth cohorts among
males. We refer to males born between 1946 and 1950 as the treatment group, and males of
adjacent cohorts of 1942–1944 and 1951–1953, as well as females in these cohorts, as control
groups, since females were not subject to the draft. Using data from the National Health
Interview Survey 1998–2003, we implement the regression discontinuity design in an
instrument-variable framework using a single indicator for the treatment group as the instrument
variable for educational attainment.
Our exploration of the difference in educational attainment level between treatment and
control groups shows that the Vietnam war draft avoidance behavior generates a strong
instrument for college completion—causing about a 5% increase in college completion rate. This
finding stands as a stark contrast to the effect of compulsory school attendance on schooling
(Angrist and Krueger 1991, Angrist and Imbens 1995). Compulsory school attendance increases
schooling for all levels of schooling: individuals born in the fourth quarter have a uniformly
higher level of schooling than those born in the first quarter.
Having established a strong instrument for college education, we examine the effect of
college education on obesity and obesity co-morbidities. The main results, shown in Table 1,
support the hypothesis that college education improves physical health: it reduces the probability
of obesity by approximately 40–60%, and reduces the probability of obesity co-morbidities—
such as hypertension, diabetes, and dental loss—by approximately 30–60%. Robust to a variety
of specification checks, our findings indicate that the traditional return to schooling estimates
that only focus on monetary earnings greatly underestimate the benefit of schooling.
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In the remainder of the paper, Section 2 reviews the literature. Section 3 describes the
data, background, and visual evidence of the quasi-natural experiment of college education.
Section 4 develops the identification strategy. Section 5 presents the results and robustness
analysis. Section 6 discusses the implications of our findings and Section 7 concludes.
2. Obesity and Education-Health Literature
Studies on adult obesity find that diet and activity both affect body weight and the
incidence of obesity, given that obesity is commonly defined as an energy imbalance created
when energy intake exceeds energy expenditure. Positive associations are found between obesity
and such factors as agricultural innovation, national economic expansion, the declining relative
price of food, the increased availability of fast food, and the increased proportion of sedentary
work.
Lakdawalla and Philipson (2002) hypothesize that technological change has raised the
cost of physical activity and lowered the cost of calories. They find that about 40% of obesity is
due to expansion of the food supply, and 60% is due to demand factors such as a decrease in
physical activity. Chou, Grossman, and Saffer (2002) find that the per capita number of
restaurants, prices of fast food and food consumed at home, plus hours of work are all important
factors that explain the trend of adult obesity. Cutler, Glaeser, and Shapiro (2003) propose that
the switch from individual to mass preparation of food leads to over-consumption because food
is less expensive to purchase and takes less time to consume. To the best of our knowledge,
however, no study has yet attempted to show the causal effect of education on obesity.
The strong and positive relationship between education and health can be interpreted in
several ways: an increase in education improves health, better health increases educational
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attainment, or an unknown “third variable” affects both education and health in the same
direction, such as genetic characteristics and/or rate of time preference (Fuchs 1982). Although
Grossman (2003) concludes that “years of formal schooling completed is the most important
correlate of good health,” after an extensive review of the literature, we argue that the existence
of a “third variable” that explains the correlation is not completely refuted. Individuals who have
lower rates of time discounts (more patient) are more likely to stay in school longer and do (or do
not do) things that contribute to better (or worse) health.
An ideal but implausible experiment to measure the effect of education on health is to
randomly assign educational attainment levels while keeping other factors constant; the
corresponding improvement in health, if any, would represent the overall positive effect of
education on health. Random assignment would eliminate the correlation between education and
unobserved health-related factors. In the absence of a true experiment (and the moral
unacceptability of creating one), a natural or quasi-natural experiment may generate instrument
variables that can be used to reduce this correlation (Arkes 2001, Adams 2002, Currie and
Moretti 2003, De Walque 2004, Grimard and Parent 2005, and Lleras-Muney 2002).
Lleras-Muney (2002) and Adams (2002) both use compulsory school law and find that
education reduces mortality (Lleras-Muney) and increases the probability of good health
(Adams). Arkes (2001) uses the state unemployment rate during a person’s teen years as the
instrument for schooling and argues that a higher unemployment rate increases incentives to
attain more education because it reduces the opportunity cost of attending school. He finds that
more years of completed schooling reduce the probability of having work-limiting health
conditions. Currie and Moretti (2003) construct an education availability measure based on the
information of college openings and use it as an instrument for education; they find that as a
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woman’s education level increases, so does her child’s birth weight. De Walque (2004) and
Grimard and Parent (2005) examine the effect of education on smoking using the Vietnam draft
avoidance behavior to instrument education, and find that education increases the probability of
never smoking, although there is little evidence that education has an impact on quitting smoking
once the habit is formed.
3. A Quasi-Natural Experiment of College Education
We use the most recent multiple waves of the National Health Interview Survey (NHIS)4.
NHIS contains standard personal and household characteristics, such as age, gender, race,
educational attainment, labor outcomes, and veteran status (based on honorable discharge status),
as well as household income, home ownership, family structure, and region of residence. In
addition to self-reported chronic conditions and physical activities, NHIS contains height and
weight data as measured by technicians. The base sample consists of all U.S.-born males and
females of cohorts between 1942 and 1953 taken from the NHIS 1998–20035. Table 2 shows the
health outcomes by categories of educational attainment, confirming that better education is
uniformly associated with decreased probability of obesity and its co-morbidities. The difference
in these health outcomes is significant between college graduates and all other categories, and
this difference persists regardless of race or veteran status.
4 NHIS is an annual nationwide probabilistic household survey of households, and focuses on the civilian, non-institutionalized population in the United States; each year since 1957, the NHIS randomly samples approximately 48,000 households comprising 108,000 individuals from 201 primary sampling units nationally. Details of NHIS are available at http://www.cdc.gov/nchs/nhis.htm. 5 The choice of birth cohorts is motivated by the regression discontinuity research design and will be discussed below. The choice of U.S.-born individuals is constrained by the fact that only male U.S. citizens were subject to be drafted during the Vietnam War, and therefore only male U.S. citizens were assigned to the treatment of using college enrollment as an effective method of draft avoidance. The choice of survey years is due to the data
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3.1. Background of the Natural Experiment of College Education
During most of the Vietnam War between 1965 and 1969, men were required to register
at their local draft board on their 18th birthday. The draft board could issue deferments for
school attendance, the existence of dependent children, and several other factors considered to
possibly cause hardship on the family, or it could classify the registrant as “available for service”
and require that he undergo a pre-induction physical. Men who passed the physical were liable to
induction and could be ordered to report for duty any time. The process of deciding which men
were drafted was set by order of the President, with highest priority for “delinquents”—those
who failed to register or failed to report for the pre-induction physical; second priority went to
volunteers; and third priority was for non-volunteers between the ages of 19 and 25.
Since few men between the ages of 26 and 35 were ever drafted, men who were able to
maintain a college deferment until their 26th birthday could effectively avoid the draft, even
though they were technically eligible for induction until age 35. Men could also apply for a
graduate deferment and occupational or dependent deferments until 1968. The number of
educational deferments was large: there were 1.703 million college deferments and 0.526 million
high school deferments in 19676.
Figure 1 shows the induction statistics by draft years. The peak draft years were between
1965 and 1969; the number of males drafted decreased sharply in 1970 and disappeared in 1973
when the draft ended. During the peak draft years, cohorts 1946–1950 were aged appropriately
for both college and the draft, so these cohorts had the highest incentives to use college
education as an effective means to avoid the draft.
limitations in the NHIS 1969–1997, which do not contain birthplace information. We use the base sample throughout the analysis, unless specified otherwise. 6 With the institution of a draft lottery in 1970, deferments for educational reason became more difficult to obtain, particularly for graduate studies. Deferments for college and high school continued, but at a greatly decreased rate.
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3.2. Visual Evidences
Figure 2a graphically demonstrates that one unintended consequence of this historic
event is to effectively serve as a “natural experiment” of the effects of education among all non-
veterans, including females. It is evident from the figure that there is a sharp rise in males’
college graduation rates in cohorts 1946–1950, followed by a sharp fall in cohorts 1951–1953,
but this “rise and fall” is clearly absent in females of the same cohorts. Similarly, the gender
difference in college completion rate is clearly wider in cohorts 1946–1950 (hereafter, treatment
cohorts), whether it is compared to that of earlier cohorts of 1941–1944 (hereafter, older control
cohorts) or later cohorts of 1951–1953 (hereafter, younger control cohorts). The visual evidence
confirms that males in cohorts 1946–1950 received an additional dose of college education
because those men elected to attend college in response to the exogenous induction risk that
women did not have. We obtain similar visual evidence when we focus on white non-veteran
males and females in Figure 3a.
Figures 2b and 3b display the obesity rate corresponding to this natural experiment of
college education among non-veterans of all races and white non-veterans, respectively. There is
a steady decline in males’ obesity rate in cohorts 1946–1950, and a sharp rise in cohorts 1951–
1953. Combined with the “rise and fall” in college education, this strongly suggests that college
education has a negative effect on obesity. The difference in the unadjusted mean obesity rates as
shown in both figures between these cohorts may be a noisy representation of the effect of
college education on obesity, because demographic characteristics—such as age, gender, and
race—are important determinants of obesity. For that, we turn to an econometric analysis and
formally identify and obtain accurate estimates of the impact of college education on obesity.
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4. Identification
4.1. A Regression Discontinuity Approach
The goal of a regression discontinuity design is to determine the effect that a binary
treatment variable has on an outcome variable, where the probability of receiving treatment is a
function of some observed variable V that takes a continuum of values and is discontinuous at a
known threshold7. Hahn, Todd, and van der Klaauw (2001) establish the regression discontinuity
design (RDD) identification condition when treatment status is randomly assigned: individuals
close to the threshold are similar in the absence of treatment; that is, the mean outcome for
individuals just below the threshold constitutes the valid counterfactual for those just above the
threshold. The untestable RDD identification condition when individuals self-select into
treatment status is the existence of a subgroup of individuals for whom treatment status changes
discontinuously at the threshold.
Lee (2005) develops testable identification conditions based on the assumption of the
cumulative distribution function (CDF) of the observed variable V that determines treatment
status. These assumptions are: (1) the CDF depends on some unobserved variables to allow that
individuals can have some control over their probability of treatment; (2) the CDF conditional on
the unobserved variables is bounded exclusively between 0 and 1, meaning that there is an
element of random chance in V and no individual can precisely manipulate V to determine
his/her treatment status; and (3) the CDF is continuously differentiable in the observed variable
7 There are two main types of discontinuity designs: the sharp design and the fuzzy design. In a sharp design, treatment status is determined by whether V exceeds a known threshold, while in a fuzzy design, treatment status is a random variable because its conditional probability is a function of some variable V and additional variables unobserved by the econometrician, but it is known to be discontinuous at the threshold.
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at the threshold, meaning that an individual has the same probability of obtaining a V just below
the threshold as just above it.
Three properties follow under this assumption: (1) the probability distribution of the
unobserved variables of individuals is the same just above and just below the threshold; (2) the
discontinuity gap in the conditional expectation of the outcome variable identifies a weighted-
average treatment effect for the entire population; and (3) all pre-determined characteristics that
may depend on the unobservable variable should have the same distribution just below and just
above the threshold. This last part provides a validity check of the RDD: if the distribution of any
pre-determined characteristics conditional on V changes discontinuously around the threshold,
the identification condition must not hold.
We test this identification condition and present the results for males in Table 38. We
observe no difference between treatment and control groups in household characteristics,
employment characteristics, and personal earnings and family income with two exceptions.
Compared to control cohorts, treatment cohorts have more children, are more likely to be
employed in the public sector and as skilled professionals, and the latter is likely to be driven by
educational differences. These results indicate that treatment and control cohorts do not have a
significantly different distribution of characteristics variables. That is, there is no discontinuity in
the distribution of pre-determined variables around the threshold. If we assume that treatment
and control cohorts do not differ significantly in their unobserved characteristics, we can
8 To test for the equality of the distribution of characteristics between treatment and control groups, we use Pearson and Fisher’s exact statistics for binary and categorical variables with no more than five categories, and the Kolmogorov-Smirnov test for continuous or categorical variables with more than five categories. We exclude females in the comparison because some characteristics can be systematically different in females compared to males, and therefore females may not serve as a good comparison. For example, females have different labor participation and outcomes than males.
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conclude that the RDD identification conditions are met, and that RDD is an appropriate research
design for our analysis.
4.2. A Reduced Form Model for the Total Effect of Education
There is a regression discontinuity design inherent in this quasi-natural experiment of
college education based on the background and visual evidence shown in Figures 2 and 3. We
consider the following model:
0i i i X iy d X w iβ β β ε= + + + (1)
( )1 , , ,i i i i id v w z X u 0= ≥⎡ ⎤⎣ ⎦ (2)
where i is the individual script; y denotes the outcome variable (obesity and its co-morbidities);
w, unobserved variables; X, observed variables; and ε, the error term that satisfies
[ ]| , 0i i iE w Xε = . d is an observed variable with value 1 for those who completed college and 0
otherwise. v is a latent variable that represents an individual’s potential to attend and complete
college as a means of avoiding the draft. Its value depends on induction risk z and a random
element u in addition to w that could represent an individual’s innate ability, motivation, and
efforts and X that could represent academic qualifications prior to college, parental income,
and/or other socioeconomic and demographic variables.
The critical assumption is that even though a male can influence his chance of admittance
to and completing college, there is a non-trivial random chance component in ultimately
obtaining a college degree, and that conditional on a male’s choices and characteristics, the
potential of completing college has a continuous density. For example, the quantity and quality
of college applicants in a given year and/or at a particular school may influence one’s chance of
being admitted to college that year and/or at that school, and that peers and teachers may
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similarly influence one’s chance of finishing courses and other requirements to obtain a college
degree.
We employ a linear probability specification to the education equation (2):
0i i z i X id z X w uiα α α= + + + (3)
Equations (1) and (3) constitute the reduced-form model for the non-veteran portion of the base
sample. Extending to the entire base sample that includes veterans and treating veteran status as
endogenous, we have:
i i F i Xv F X ivγ γ ε= + + (4)
i i v i i Xy d v X iyβ β β= + + +ε
(5)
where v is a veteran status dummy variable, and F is an instrument variable that is correlated
with veteran status but assumed to be uncorrelated with health outcomes. Equations (3)–(5)
constitute the estimable equations for the full base sample. The age range (between 19 and 25)
that was eligible for military duty established by the Selective Service Agency provides a natural
set of instrument variables F for veteran status. We construct a variable to represent the risk of
induction by taking the difference in age in a peak draft year, 1967, and the youngest eligible
drafting age, 19. We use quatic terms of this induction risk representation as the instrument for
veteran status9.
4.3. A Semi-Reduced Form Model for the Independent Effect of Education
To better understand the effect of college education on obesity, we examine potential
links between college education, earnings, household income, physical activity, and obesity. We
9 The instrument F for veteran status is mechanically different from the instrument variable z for college education, although it is the same idea. It thus seems that the identification of veteran status and education is based on the choice of two particular functional forms that capture the same concept.
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presume that college education leads to increased earnings and household income, which in turn
influences lifestyle behaviors such as leisure-time physical activities. We suppose that college
education may directly influence lifestyle behavior beyond its effects on earnings and income,
such as adopting a more physically active lifestyle. We suppose that college education may also
reduce obesity risk through mechanisms other than such observed lifestyle behaviors and
socioeconomic status.
To examine the empirical importance of these proposed mechanisms, we estimate the
following triangular simultaneous system of equations:
i d i i M i a i Xy d M a X iyβ β β β= + + + +ε
a
(6)
i d i i M i X ia d M Xδ δ δ= + + +ε
m
(7)
i d i i X im d Xφ φ ε= + + (8)
i i i Xd z X idα α ε= + + (9)
where m is socioeconomic status and M is a polynomial term of m, a indicates physical activity, ε
indicates various error terms, and all error terms can be correlated. Since household income may
influence an individual’s preference structure for health, and consequently, health behaviors as
inputs to health, we include a cubic term of income in the obesity equation to allow its effect on
obesity to be flexible in (6)10.
4.4. RDD Estimation
Difference-in-difference estimators and several non-parametric and semi-parametric
procedures are available to implement a regression discontinuity design. For example, Lee
10 A limitation of system equations (4)–(7) is that the identification of equation (4) is based on the instrument for education and functional form, i.e., using a polynomial of incomes and an imposed diagonal structure, although our instrument allows us to identify the role of education on income and physical activity in (5)–(6).
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(2005) uses polynomial approximations to generate the estimates of the discontinuity gap, and
Hahn, Todd, and van der Klaauw (2001) suggest local linear regression. Both difference-in-
difference estimators and local linear regression are numerically equivalent to an IV estimator
where we control for linear trend and the instrument is an indicator for the treatment group.
Our dependent variable is obesity versus lean (“obesity” for short), which is set to 1 if the
individual has a BMI of 30 or higher (a marker of obesity) and 0 if the individual has a BMI less
than 25 (a marker of leanness). College education is a dummy that is set to 1 if an individual has
a college degree or higher and 0 otherwise. The instrument variable for college education is an
interaction term of two dummies: male and birth cohort 1946–1950. In addition, we control for
the mean shift in female college education and obesity rate between treatment and control groups
by using a dummy variable is4244 (is5153) that is set to 1 for the older (younger) control cohorts
and 0 otherwise11. Our model assumes that the covariate that determines the treatment status is
continuous. However, since birth year is not continuous, it is theoretically infeasible to compare
outcomes for observations just above and just below the treatment threshold. We employ the
procedure developed in Lee and Card (2004) to amend this problem by clustering at the age cell
level, specifically, the interaction term of age and male dummy, to obtain the robust standard
errors.
11 In all specifications, we control for male dummy; quatic terms of age; quatic terms of interaction of age and male dummy; unrestricted survey year dummies; interaction terms of age and survey year dummies; triple interaction terms of age, male, and survey year dummies; and region dummies. In specifications that include non-white individuals, we additionally control for interaction terms to allow the college education effect to vary between white and non-white populations. They are quatic terms of the triple interaction terms of age, male, and white dummies; interaction terms of white and male dummies; and quadruple interaction terms of age, male, white, and survey year dummies.
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5. The Results
5.1. Does Draft Avoidance Increase Education? The Validity Check of Our Instrument
To better understand how this draft avoidance behavior constitutes a quasi-natural
experiment that generates an instrument for education, we explore the difference in educational
attainment level between the most affected males and those who were affected less or not at all,
including females and other males of adjacent cohorts. We assess whether our instrument meets
the monotonicity condition: one is more likely to enroll in college as a means of avoiding the
draft when at risk of being drafted than when not at risk of being drafted. Since we use females
as controls, the monotonicity is that the male-female college enrollment difference in treatment
cohort is greater than that in the control cohort. Though not verifiable, the monotonicity implies
that the cumulative distribution function (CDF) of male-female difference in years of schooling
of the treatment group should lie uniformly below that of the control group (Angrist, Imbens, and
Rubin 1996).
Figure 4 and 5 graph the male-female difference in the CDFs of years of schooling in
treatment and control cohorts. Figure 4 also shows the difference between the two for non-
veterans and Figure 5 shows the difference among individuals including veterans. It is clear that
relative to females, the draft avoidance behavior induced a large increase in males’ schooling at
levels of high school graduation, college attendance, and associate degrees regardless of race or
veteran status. Furthermore, the draft avoidance behavior induced a large increase in college
completion only among non-veterans, which is expected, because veterans have lower college
completion rates than non-veterans. Evidence in these figures shows that our instrument variable
is a valid instrument only for the educational attainment levels that meet the monotonicity
condition: college completion, college enrollment, associate degree or higher, and high school
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graduation. This stands as a stark contrast to compulsory school attendance (Angrist and Krueger
1991, Angrist, Imbens, and Rubin 1996): compulsory schooling law increases educational
attainment uniformly for all the levels of schooling with the largest increase between grade eight
and high school graduation.
To complement the visual evidence for monotonicity, we present the first-stage estimates
of the instrument variable for various education levels in Table 4 for our treatment group of
males born in between 1946 and 1950 using (1) females of cohort 1946–1950 and (2) males and
females of cohorts 1942–1944 and 1951–1953 as control groups. To allow the effect of the
instrument on education to vary across race and veteran status, we present the estimates
separately for white non-veterans, all non-veterans, all whites, and all individuals. We also
control for the mean shifts among females between treatment and control groups.
We find that our instrument is a strong predictor for college education—an approximate
5% increase in college completion rate regardless of race and the endogenous veteran status12.
Among all non-veterans, our instrument is valid for other educational attainment levels: we see
about a 4% increase in associate degree or higher, a 3% increase in having attended college, 0.17
more years of schooling beyond high school, and 0.22 years of total completed schooling. There
is no difference between treatment and control groups in their probability of graduating from
high school or completing the 11th grade or lower. This is as expected, because it is consistent
with how the draft avoidance behavior generated the instrument variable—many college-aged
males who were also draft-eligible enrolled in college to avoid the draft.
As an additional piece of evidence, Table 3 compares the distribution of several measures
of educational attainment between males in treatment and control cohorts. While the treatment
12 We use linear probability specification for all measures of educational attainment except for years of completed schooling. The probit estimation yields similar results.
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group has more years of schooling than the control group has, the increased years of schooling is
contributed solely by the increase in those who attended and/or finished college, because there is
no difference between the treatment and control groups in schooling among those who never
attended college. Furthermore, the increased rate of having attended college is contributed solely
by the increased rate of having completed college, because there is no difference in years of
schooling among those attended college but did not complete college.
5.2. Does College Education Reduce Obesity? The Basic Results and Robustness Checks
Table 1 presents the estimates of the effect of college education on obesity. The IV
estimates of college completion are large and significant, particularly among white individuals:
having completed college reduces the chance of obesity by 60% among non-veteran whites and
61% among all whites. When non-white individuals are included, having completed college
reduces the chance of obesity by 44% among all non-veterans and 50% among all individuals.
The ordinary least square (OLS) estimates confirm the strong negative relationship between
education and obesity: having completed college is associated with approximately a 14–15%
reduction in obesity. We find that there is a shift of mean among females between treatment and
control cohorts in college completion and obesity rate that is induced by other exogenous factors:
control cohorts have lower college completion and obesity rates than treatment cohorts.
Among a battery of robustness checks, we first examine whether there is heterogeneity in
the receipt of treatment, and more importantly, whether our results are sensitive to this potential
heterogeneity. Instead of assuming that the treatment group has a uniform increased chance of
completing college by using a single instrument variable—males born between 1946 and 1950—
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as an instrument for college education, we approach the treatment heterogeneity in the choice of
treatment cohorts and of instrument variables.
In Table 5, we use a narrower set of treatment cohorts to capture the peak years of draft
avoidance behavior such as cohorts 1947–1950, 1946–1949, and 1946–194813. We find that the
instrument variable resulting from these alternative choices of treatment cohorts remains a strong
predictor for college education. For example, among the white non-veterans, the difference in
college completion rate between treatment and control groups is the largest—5.60%—for the
narrowest range of cohorts 1946–1948, and smallest—4.35%—for the widest range of cohorts
1945–1950. We see a similar pattern among all non-veterans. The IV estimate of the effect of
college education on obesity becomes slightly larger in magnitude when we use narrower ranges
of treatment cohorts, as well as when we expand the treatment group to include 1950, which is
defined as a transitional cohort in the baseline estimates.
As an alternative to capturing the heterogeneity, we use multiple instrument variables to
instrument college education: males born in 1946, males born in 1947, males born in 1948, males
born in 1949, and males born in 1950, instead of grouping them into a single instrument variable
of males born between 1946 and 1950. We find some evidence of cohort-specific heterogeneity
in the increase in college completion between treatment cohort and control groups. For example,
among all non-veterans, males born in 1946 are 5.79% more likely and males born in 1947 are
6.43% more likely than those in the control groups to have completed college. We also find some
evidence of race-specific heterogeneity in the receipt of the treatment. For example, the
difference in college completion rates between non-veteran white males born in 1946 and those
born in control cohorts is 7.32% while the difference between all non-veteran males born in 1946
13 We reduce the size of the treatment group by eliminating observations of the cohorts of 1946, 1950, and 1949–1950 for the alternative sets of treatment cohorts 1947–1950, 1946–1949, and 1946–1948, respectively.
Page 19
and those born in control cohorts is 5.79%; for cohorts 1947 and 1948, the increased college
completion rate is greater among all non-veterans than among white non-veterans.
We next investigate two specification issues: the inclusion of additional individual
covariates, and any unobserved household effects that may influence obesity. We present the
results in Table 6. First, as an additional test of the RDD identification assumption that pre-
determined characteristics are similar between treatment and control groups, we include a
number of characteristics variables14. If the RDD is an appropriate research design, the estimate
of effect of college education should be resilient to the inclusion of characteristics variables.
Among the white non-veterans, the first-stage coefficient estimate for the instrument variable is
0.0562, slightly higher than the 0.0534 estimate without these additional covariates;
consequently, the effect of college education on obesity is –0.5984, slightly lower than the –
0.6055 estimate without these additional covariates. We obtain similar results for all non-
veterans.
Second, one may be concerned with the possible influence of unobserved household
effects, such as shared attitudes and beliefs about diet, physical activity, and other health-related
lifestyles. To control for the contribution of unobserved household factors, we construct a
pseudo-panel where a household is scripted as an individual unit and household members are
scripted as a time unit for a given individual; we then perform the panel estimation treating the
household effect first as a random effect and then as a fixed effect. Among the white non-
veterans, we find that the random effect estimate remains nearly unchanged: the first-stage
coefficient estimate for the instrument variable is 0.0534 and the effect of college education on
14 Characteristics variables include: marital status (seven categories), housing (own, rent, and other), family type (four categories), family size, number of children under 18, and number of elders in the household.
Page 20
obesity is –0.6110, while the fixed-effect estimate is insignificant. The Hausman test shows that
the random effect specification is adequate for modeling the unobserved household effect.
Continuing with the robustness analysis, we examine two heterogeneity issues of the
effect of education on reducing obesity: whether it varies by level of leanness and educational
attainment or leanness. For the purpose of brevity, we present the results for white non-veterans
in Table 7. First, instead of comparing the obese (BMI ≥ 30) with the lean (BMI < 25), we
compare the obese with alternative levels of leanness: BMI < 26, BMI < 27, BMI < 28, BMI <
30, and finally, with normal weight: BMI between 18.5 and 25. The first row of Table 6 indicates
that the effect of college education on reducing obesity is insensitive to the alternative levels of
leanness.
Second, we examine whether the effect of education on obesity varies by educational
attainment level. The first column of Table 7 provides suggestive evidence that the effect of post-
secondary education on obesity not only varies by attainment categories but also exhibits non-
linearity. For example, college completion reduces obesity by about 60%, while having an
associate degree or higher reduces obesity by over 80%, and each additional year beyond high
school reduces obesity by over 18%. This pattern is extended to alternative definitions of
leanness.
5.3. How Does College Education Reduce Obesity? Potential Mechanisms
We investigate potential mechanisms through which college education reduces obesity.
Two main explanations on how education improves health are that education increases an
individual’s efficiency in health inputs allocation (Grossman 1972, Grossman and Kaestner
1998) and in health production (Grossman 1972). The allocative efficiency explanation has been
Page 21
extensively studied and is consistently supported by the education-smoking literature; however,
there are fewer studies on the effect of education on inputs related to body weight. The
productive efficiency explanation argues that education provides individuals with critical
thinking skills that are useful in the production of health. For example, more educated
individuals are better able to manage chronic conditions (Goldman and Lakdawalla 2001) and
more likely to comply with treatments for diabetes and AIDS (Goldman and Smith 2001) than
less educated individuals.
We estimate the system of simultaneous equations (4)–(7) that take into account the
endogenous effects of personal earnings, family income, and physical activity using three-stage
least square. We find that in their leisure time, college graduates are nearly twice as likely than
non-college graduates to engage in physical activity on a regular basis. Personal earnings reduce
an individual’s chance to engage in physical activities, though its effect is insignificant: high
personal earnings present a great opportunity cost of spending leisure time on physical activity.
Household income has no significant effect on physical activity after college education, personal
earnings, and other covariates are accounted for.
We find household income has a strong and significant effect on obesity, and the effect is
multifaceted—the sign and the convexity of the effect changes across income categories. College
education exerts an independent effect on reducing obesity above and beyond its effects through
personal earnings, family income, and physical activity. Holding personal earnings and
household income steady, those who completed college are 151% less likely to be obese than
those who did not. Our results suggest that college education reduces obesity through allocative
efficiency.
Page 22
5.4. College Education and Obesity Co-Morbidities
Obesity is a public health issue because it is associated with many diseases, including
hypertension and Type 2 diabetes15. We want to examine whether college education has a similar
protection on obesity co-morbidities, and present the results in Table 8. We find that college
education reduces the chance of being diagnosed with diabetes at middle age (age 45) by
approximately one-fifth to one-third. The estimates are stronger when we include veterans,
though being a veteran has a positive but insignificant effect on diabetes. The two distinctive
forms of diabetes—those that are insulin-dependent and those that are insulin-independent, or,
loosely speaking, Type 1 and Type 2, respectively—allow us to perform a falsification test. If
college education has a causal effect on reducing diabetes, it should have an effect on insulin-
independent diabetes that is a common co-morbidity of obesity, but not on insulin-dependent
diabetes that is not associated with obesity. Our results are exactly what we expect: the effect of
college education continues to be significant and strong on insulin-independent diabetes, but
becomes insignificant on insulin-dependent diabetes.
We find that college education reduces the chance of being diagnosed with hypertension,
and the effect is strongest among whites and all individuals: in both groups, it reduces the chance
of hypertension by half. We also find that hypertension is more prevalent among veterans than
among non-veterans: the difference between veterans and non-veterans is 32% among whites and
41% among all races after college education and demographics are controlled for.
15 Overweight and obese individuals are at increased risk for many diseases and health conditions, including hypertension, dyslipidemia (for example, high total cholesterol or high levels of triglycerides), Type 2 diabetes, coronary heart disease, stroke, gallbladder disease, osteoarthritis, sleep apnea, respiratory problems, and some cancers (e.g., endometrial, breast, and colon). U.S. Department of Human and Health Service.
Page 23
One may be concerned with the potential bias of omitted variables such as health care
access and utilization in our estimates of college education on obesity co-morbidities, though the
co-morbidities we have examined are diagnosed by health professionals, indicating some level of
access to health care. We address the potential omitted variable bias issue by examining the
effect of college education on an obesity-related health outcome that is definitely related to
health care: dental loss.
Without controlling for dental care access or utilizations, college education reduces the
chance of complete dental loss and that effect is particularly strong among whites, where it
reduces the chance of complete dental loss by nearly one-third. We examine the effects of (1)
dental care affordability—whether one did not see a dentist because he/she couldn’t afford to,
and (2) dental care utilization—whether one never saw a dentist for any reason—on our
estimates of college education. We find that dental care affordability is an important determinant
and that dental care utilization is not. The estimate of the effect of college education on dental
loss is insensitive to the inclusion of the effects of dental care. For the purpose of comparison,
we present the estimates when we treat veteran status as exogenous because the correlation
between dental loss and the unobserved factors that led one to be a veteran may be negligible.
The effect of college education continues to be strong and significant among non-veterans, and
among individuals including veterans.
We investigate whether the effect of education on obesity co-morbidities varies by
educational attainment level. Results in Table 9 provides suggestive evidence that the effect of
post-secondary education on obesity not only varies by attainment categories but also exhibits
non-linearity. For example, among white non-veterans, the effect of college completion on
reducing insulin-independent diabetes is 17%, of having an associate degree or higher is 22%,
Page 24
and of each additional year beyond high school is 5%. There is a similar pattern on hypertension
and dental loss across race and veteran status.
6. Discussion
That the IV estimate of the effect of college education on obesity is larger than the OLS
estimate can be interpreted as follows: our instrument variable is generated by the natural
experiment that affected the choice of college completion of individuals who would not have
completed college in the absence of the inadvertent experiment. If different people face different
health returns to college education, the IV estimate reflects the marginal rate of return to the
group affected by the experiment. That is to say, the IV estimates do not generalize to the
average return in the entire population, and the health return to college education is greater
among those affected than the those not affected16. From a policy perspective, the marginal
return is more relevant than the average return because the efficacy of a policy such as college
tuition relies on the return among those who may be affected by the policy.
Our findings indicate that the traditional return to schooling estimates that only focus on
monetary earnings greatly underestimate the benefits of college education. Obese Americans cost
the country about $75 billion in weight-related medical bills in 2003, and the public paid about
$39 billion or about $175 per taxpayer through Medicare and Medicaid programs for obesity-
linked illnesses (Obesity Research 2005). With about 60 million obese adults and 9 million obese
children in the U.S., the annual medical cost of obesity is over $1,000 per obese person, which
amounts to a present value of over $20,000 using the discount rate of 5%. In the United States,
16 This interpretation originates from Card 2001. There are two other plausible explanations: (1) measurement error in the college completion variable that leads a downward bias of the OLS estimate, and (2) the presence of social externalities of college education such that one’s obesity depends not only on his own college education, but also on that of the people with whom he interacted.
Page 25
the per-student cost of post-secondary education was $22,234 in 2001 (OECD 2005). The benefit
of college education on reduced obesity risk and consequently reduced obesity-related medical
bills alone would be sufficient to finance the college education.
One limitation of our study is the potential confounding influence of intelligence that our
estimation does not control for because NHIS lacks measures of intelligence. Educational
attainment level and intelligence are usually positively correlated, but including a control for
intelligence in earnings regressions does not have a significant effect on the education
coefficient. One study of health differences among the elderly with chronic conditions finds that
including intelligence test scores eliminates the significance of the education variable (Fuchs
2004).
7. Conclusions
The close tie between the natural age of college attendance and the draft during the
Vietnam war era creates a quasi-natural experiment that we exploit to study the effect of draft
avoidance behavior on college education and the effect of college education on obesity and
related health outcomes. Because of the college deferments issued by the government during this
era, males born in the years between 1946 and 1950 who faced the greatest induction risk
enrolled in college as an effective means of avoiding being drafted. We verify that this natural
experiment resembles a regression discontinuity research design, and the use of the regression
discontinuity design allows us to identify the causal effect of college education on obesity under
a weaker condition than the exclusion restriction in the classical IV estimation: individuals could
have some, but not complete, control over their chance of completing college.
Page 26
We explore the difference in educational attainment level between the males most
affected males and those who were less affected, or not affected at all, including females and
males of adjacent cohorts. In contrast to compulsory school attendance (Angrist and Krueger
1991), we find that Vietnam war draft avoidance behavior generates a strong instrument for post-
secondary education—causing about a 5% increase in college completion, but no increase for
grades below high school.
Our results support the hypothesis that college education improves physical health: it
reduces the probability of obesity by approximately 40–60%, and reduces the probability of
obesity co-morbidities such as hypertension, insulin-independent diabetes, and complete dental
loss by approximately 30–60%. Robust to variety of specification checks, our findings indicate
that the traditional return to schooling estimates that only focus on monetary earnings greatly
underestimate the benefits of schooling.
Page 27
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Table 1: Main Results of the Effect of College Education on Obesity and Obesity Co-Morbidities
White Non-Veterans(1)
All Non-Veterans(2)
All Whites(3)
All(4)
OLS IV OLS IV OLS IV OLS IV
First-Stage for College
0.0534 *** (0.0206)
0.0550 *** (0.0182)
0.0044 (0.0304)
0.0317 * (0.0189)
Obesity –0.1495 *** (0.0117)
–0.6055 ** (0.2711)
–0.1375 *** (0.0109)
–0.4386 ** (0.2487)
–0.1474 *** (0.0104)
–0.6089 ** (0.2973)
–0.1340 *** (0.0099)
–0.5058 **
(0.2406)
Diabetes –0.0280 *** (0.0034)
–0.1775 * (0.1060)
–0.0258 ***(0.0032)
–0.1940 * (0.1189)
–0.0265 ***(0.0033)
–0.3225 * (0.1803)
–0.0248 ***(0.0030)
–0.5284 **
(0.2440)
Hypertension –0.0651 *** (0.0067)
–0.3727 (0.3246)
–0.0714 ***(0.0061)
–0.7706 (6.3744)
–0.0697 ***(0.0058)
–0.5395 * (0.3236)
–0.0737 ***(0.0053)
–0.5698 **
(0.2812)
Dental Loss –0.0865 *** (0.0047)
–0.3820 *** (0.1398)
–0.0875 ***(0.0045)
–0.3240 *** (0.1174)
–0.0890 ***(0.0041)
–0.4231 (0.2724)
–0.0878 ***(0.0039)
–0.5450 **
(0.2531)
N 13,424 16,357 15,761 19,143
Notes: Data source is the National Health Interview Surveys 1998–2003. The sample contains U.S. born birth cohorts 1942–1953. Obesity is 1 if one’s BMI >= 30 and 0 if one’s BMI < 25, where BMI is the ratio of body weight in kilogram and the square of height in meters. Diabetes (Hypertension) is whether one was diagnosed for diabetes or board-line diabetes (hypertension on at least two different visits). Dental loss is whether one lost all permanent teeth. College education is whether one has a college degree or higher, and is instrumented by being a male born in 1946–1950. N is the sample size of obesity, varies slightly for other outcomes because of missing observations. All estimates control for control cohort dummies, male dummy, quatic terms of age, quatic terms of interaction of age and male, unrestricted survey year dummies, interaction of age and survey year, triple interaction of age, male and survey year, and region. Robust standard errors are in parentheses and obtained by clustering at interaction term of age and male. Columns (3)–(4) also use quaric terms of interaction of male and age over draft age (19) on draft year 1967 to instrument veteran status. Columns (2) and (4) also control for quatic terms of triple interaction of age, male and white; and quadruple interaction of age, male, white and survey year. ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level;.
Page 30
Table 2: Obesity and Its Co-Morbidities Rates by Educational Attainment
White Non-Veterans Non-Veterans Whites All
Obesity vs. Lean
H.S. Dropouts 0.3447 (0.0092) 0.3733 (0.0078) 0.3416 (0.0085) 0.3671 (0.0072)
H.S. Graduates 0.2917 (0.0063) 0.3038 (0.0057) 0.2921 (0.0057) 0.3021 (0.0052)
Some College 0.2833 (0.0060) 0.2992 (0.0056) 0.2867 (0.0054) 0.2991 (0.0049)
College Graduates 0.2025 (0.0052) 0.2165 (0.0050) 0.2048 (0.0048) 0.2181 (0.0046)
Hypertension
H.S. Dropouts 0.3529 (0.0090) 0.4009 (0.0077) 0.3556 (0.0084) 0.4023 (0.0072)
H.S. Graduates 0.2679 (0.0060) 0.2978 (0.0056) 0.2719 (0.0054) 0.3004 (0.0051)
Some College 0.2461 (0.0057) 0.2736 (0.0053) 0.2568 (0.0051) 0.2812 (0.0047)
College Graduates 0.2050 (0.0051) 0.2172 (0.0050) 0.2071 (0.0047) 0.2200 (0.0045)
Diabetes
H.S. Dropouts 0.1087 (0.0060) 0.1143 (0.0052) 0.1064 (0.0056) 0.1130 (0.0048)
H.S. Graduates 0.0596 (0.0032) 0.0642 (0.0030) 0.0613 (0.0030) 0.0660 (0.0028)
Some College 0.0523 (0.0030) 0.0590 (0.0028) 0.0559 (0.0027) 0.0623 (0.0026)
College Graduates 0.0310 (0.0022) 0.0361 (0.0023) 0.0347 (0.0021) 0.0394 (0.0021)
Dental Loss
H.S. Dropouts 0.2449 (0.0090) 0.2177 (0.0072) 0.2450 (0.0083) 0.2190 (0.0067)
H.S. Graduates 0.0990 (0.0044) 0.0999 (0.0040) 0.1032 (0.0041) 0.1045 (0.0037)
Some College 0.0565 (0.0033) 0.0593 (0.0031) 0.0627 (0.0031) 0.0636 (0.0029)
College Graduates 0.0214 (0.0020) 0.0217 (0.0019) 0.0233 (0.0019) 0.0236 (0.0018)
N 19,470 23,780 23,889 29,007
Notes: See notes in Table 1. Data source is the National Health Interview Surveys 1998–2003. The sample contains U.S. born birth cohorts 1942–1950. Sample size corresponds to obesity versus lean, and varies slightly for other outcomes because of missing observations. Standard errors are in parentheses.
Page 31
Table 3: Comparison of Individual Characteristics Between Treatment and Control Cohorts
White Males All Males Characteristics Variables Fisher KS Fisher KS
Household Characteristics 0.451 - 0.186 -
Marital status a (married, widowed, divorced or separated, never married, living with partner)
0.870 - 0.776 -
Housing (own, rent, other) 0.451 - 0.186 -
Family size (1–12) - 0.359 - 0.292
No. children (0–10) - 0.058 - 0.027
Region of residence (4) 0.215 - 0.204 -
Employment Outcomes
Ever worked 0.227 - 0.280 -
Employer type (private, public, self) 0.023 - 0.045 -
Hourly paid 0.203 - 0.201 -
Industry a - 0.137 - 0.124
Occupation a - 0.040 - 0.050
Job had sick pay 0.202 - 0.201 -
Had more than one job 0.728 - 0.852 -
Personal earnings b (11) - 0.513 - 0.265
Total family income b (11) - 0.360 - 0.271
Educational Attainment
Years of schooling (0–20) - 0.000 - 0.000
Years of schooling among non-college graduates (0–14)
- 0.146 - 0.534
Had some college or more 0.000 - 0.000 -
Had some college among non-college graduates
0.758 - 0.978 -
Had completed college 0.000 - 0.000 -
Notes: See notes in Table 1. Presented are the p-values of test statistics. Fisher’s exact tests are performed with binary variables, and categorical variables with no more than 5 categories. KS stands for Kolmogorov-Smirnov test for equality of distribution functions. Characteristic variables are dummies, unless it is indicated with a parenthesis showing the categories, or the range of integer-valued variables. a: Industry and Occupation Classification http://www.census.gov/hhes/www/ioindex/view.html. b: Personal earnings and family income are previous year’s and in U.S. dollars with the following eleven categories: 1–4,999, 5,000–9,999, 10,000–14,999; 15,000–19,999; 20,000–24,999; 25,000–34,999; 35,000–44,999; 45,000–54,999; 55,000–64,999, 65,000–74,999, 75,000+.
Page 32
Table 4: Validity Check of the Instrument Variable for Various Educational Levels
Educational Levels White Non-Veterans All Non-Veterans White All IV Trend IV Trend IV Veteran IV Veteran
Graduate degree 0.0044 (0.0129)
–0.0389 ***(0.0109)
0.0022 (0.0111)
–0.0362 *** (0.0098)
–0.0140(0.0126)
0.0960 (0.1249)
–0.0057 (0.0131)
–0.0091 (0.1319)
College degree and above
0.0496 *** (0.0158)
–0.0298 * (0.0165)
0.0531 *** (0.0141)
–0.0301 ** (0.0136)
0.0326 *(0.0175)
–0.1603(0.1755)
0.0554 ** (0.0231)
–0.4215 *(0.2485)
Associated degree and above
0.0399 *** (0.0154)
–0.0066 (0.0180)
0.0440 *** (0.0133)
–0.0073 (0.0174)
0.0267 (0.0190)
–0.0761(0.2093)
0.0479 ** (0.0203)
–0.2618 (0.2081)
College enrollment 0.0186 (0.0145)
–0.0020 (0.0163)
0.0298 ** (0.0127)
–0.0082 (0.0136)
0.0201 (0.0162)
–0.0549(0.1789)
0.0704 *** (0.0254)
–0.6012 *(0.3304)
Years of schooling beyond H.S.
0.1510 * (0.0815)
–0.1641 ** (0.0760)
0.1739 *** (0.0704)
–0.1608 ** (0.0678)
0.0509 (0.0907)
–0.0862(0.9394)
0.1427 (0.0910)
–0.9131 (0.8964)
Years of schooling beyond 11th grade
0.1460 * (0.0869)
–0.1470 * (0.0839)
0.1847 *** (0.07400)
–0.1537 ** (0.0773)
0.0628 (0.0936)
–0.0778(0.9710)
0.1609 * (0.0950)
–0.8746 (0.9430)
Years of schooling 0.1336 (0.0982)
–0.1874 * (0.1064)
0.2169 *** (0.0846)
–0.2025 ** (0.1040)
0.0758 (0.1053)
–0.3325(1.0932)
0.1598 (0.1143)
–0.6794 (1.0940)
H.S. graduates
–0.0050 (0.0113)
0.0171 (0.0158)
0.0106 (0.0110)
0.0071 (0.0157)
0.0118 (0.0116)
0.0083 (0.1147)
0.0181 (0.0157)
0.0384 (0.1530)
11th grade
0.0008 (0.0081)
–0.0169 (0.0127)
0.0090 (0.0095)
–0.0231 * (0.0134)
0.0063 (0.0081)
–0.0775(0.0843)
0.0003 (0.0114)
0.0546 (0.1167)
10th grade
–0.0036 (0.0083)
–0.0134 (0.0115)
0.0035 (0.0091)
–0.0183 (0.0113)
–0.0051(0.0075)
0.0475 (0.1649)
–0.0106 (0.0118)
0.1664 (0.1067)
N 20,401 24,866
Notes: See notes in Table 1. The dependent variable is educational attainment in various measures, and it a binary variable except when education is measured as years of schooling. Presents are coefficients of the instrument variable—males born in between 1946 and 1950 and mean shifts between treatment and control cohorts using the first-stage specification and base sample in Table 1. ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.
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Table 5: Robustness of College Education Estimates to Treatment Heterogeneity
Treatment group specifications White Non-Veterans All Non-Veterans
First-stage IV Estimate First-stage IV Estimate
Males of 1946–1950 (baseline) 0.0534 *** (0.0206)
–0.6055 ** (0.2711)
0.0550 *** (0.0182)
–0.4386 ** (0.2487)
N 13,424 16,357
Males of 1947–1950 0.0442 ** (0.0202)
–0.8645 *** (0.2917)
0.0504 *** (0.0194)
–0.4725 ** (0.2350)
N (after excluding cohort 1946) 12,368 15,072
Males of 1946–1949 0.0511 ** (0.0224)
–0.7814 ** (0.3087)
0.0513 *** (0.0173)
–0.4974 * (0.2512)
N (after excluding cohort 1950) 12,188 14,846
Males of 1946–1948 0.0560 ** (0.0244)
–0.6552 * (0.3550)
0.0599 *** (0.0216)
–0.5934 ** (0.2837)
N (after excluding 1949–1950) 10,986 13,366
Males of 1945–1950 0.0435 ** (0.0209)
–0.8550 ** (0.3671)
0.0434 *** (0.0184)
–0.5711 * (0.3151)
N 13,424 16,357
Multiple instrument variables
Male born in 1946 0.0732 ** (0.0322)
0.0579 ** (0.0285)
Male born in 1947 0.0422 (0.0322)
0.0643 ** (0.0283)
Male born in 1948 0.0413 (0.0314)
0.0460 * (0.0278)
Male born in 1949 0.0536 * (0.0300)
0.0552 ** (0.0264)
Male born in 1950 0.0518 * (0.0304)
–0.6029 ** (0.2780)
0.0516 ** (0.0267)
–0.4683 ** (0.2121)
N 13,424 16,357
Notes: See notes in Table 1.
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Table 6: Robustness of College Education Estimates to Specification Choices
Specifications White Non-Veterans
Non-Veterans
White All
Baseline
First-stage for college education 0.0534 *** (0.0206)
0.0550 ***(0.0182)
- -
IV estimate of college education –0.6055 ** (0.2711)
–0.4386 ** (0.2487)
–0.6089 ** (0.2973)
–0.5058 ** (0.2406)
Controlling for individual covariates
First-stage for college education 0.0562 *** (0.0202)
0.0543 *** (0.0179)
- -
IV estimate of college education –0.5984 ** (0.2906)
–0.4153 ** (0.2268)
–0.6684 * (0.3466)
–0.4276 * (0.2430)
Controlling for unobserved household effect
Random household effect
First-stage for college education 0.0534 *** (0.0206)
0.0553 *** (0.0182)
- -
IV estimate of college education –0.6110 ** (0.3028)
–3.0401 ** (0.9219)
–0.7571 ** (0.3734)
–0.2519 (0.3204)
Fixed household effect
First-stage for college education 0.0918 (0.0723)
0.1199 ** (0.0576)
- -
IV estimate of college education –0.6003 (0.7627)
–0.3264 (0.4451)
–0.4337 (0.5318)
–0.2522 (0.2856)
N 13,424 16,357 15,761 19,143
Notes: See notes in Table 1. The specification and the sample is as the same as in that in Table 1. ***: significant at 1% level and **: significant at 5% level.
Estimates with additional individual covariates include marital status (7 categories), major activity (work, housekeeping and other), housing (own, rent and other), family type (4 categories); as well as family size, number of children under 18, and number of elders present in the household.
The Hausman test statistics for testing the adequacy of modeling unobserved household effect using random effect rather than fixed effect is χ2(25) = 11.49 with p-value = 0.99 for white individuals and χ2(25) = 20.50 with p-value = 0.88 for all individuals.
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Table 7: Heterogeneity of Education Effect on Various Measures of Obesity Among White Non-Veterans
Obese vs. Lean
Obese vs. Normal Weight
Obese vs. BMI<26
Obese vs. BMI<28
Obese vs. BMI<29
Obese vs. Not Obese
College degree and above –0.6055 ** (0.2711)
–0.6416 ** (0.2712)
–0.5880 ** (0.2808)
–0.6279 ** (0.2600)
–0.4551 * (0.2325)
–0.3624 (0.2209)
Associated degree and above –0.8765 * (0.4489)
–0.6942 (0.4254)
–0.7569 * (0.4266)
–0.7645 * (0.4040)
–0.6905 * (0.4146)
–0.3929 (0.2731)
College enrollment –1.6379 (0.0163)
–1.7686 (1.1976)
–1.2262 * (0.7006)
–1.3359 * (0.7952)
–0.8405 (0.5355)
–0.6453 (0.5000)
Years of schooling beyond H.S.
–0.1821 * (0.0972)
–0.1644 * (0.0874)
–0.2340 * (0.1213)
–0.1878 ** (0.0923)
–0.1390 * (0.0897)
–0.1195 (0.0737)
Years of schooling beyond 11th grade
–0.1819 * (0.0958)
–0.1641 * (0.0856)
–0.2480 * (0.1203)
–0.1870 ** (0.0878)
–0.1390 * (0.0761)
–0.1251 * (0.0708)
Years of schooling –0.1076 (0.1284)
–0.1155 * (0.0590)
–0.2595 (0.1401)
–0.1778 * (0.0900)
–0.1259 (0.0762)
–0.1712 (0.1032)
N 13,424 13,155 15,740 17,147 19,301 19,470
Notes: See notes in Table 1. ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.
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Table 8: IV Estimates of the Effect of College Education on Obesity Co-Morbidity:
Obesity Co-Morbidity White Non-Veteran Non-Veteran White All
College College College Veteran College Veteran
Diabetes –0.1982 * (0.1135)
–0.2301 * (0.1212)
–0.3095 * (0.1751)
0.0609 (0.1131)
–0.3269 **(0.1633)
0.0821 (0.1006)
N
19,786 23,952 24,146 29,083
Insulin-independent Diabetes –0.1775 *
(0.1060) –0.1940 *
(0.1189) –0.3225 *
(0.1803) 0.1085
(0.0909) –0.5284 **
(0.2440) 0.1810
(0.1168)
N 19,645 23,744 23,946 28,828
Insulin-dependent Diabetes –0.1246(0.0847)
–0.0712(0.2983)
–0.1806(0.1234)
–0.0023 (0.0642)
–0.1542(0.1089)
–0.0069 (0.0465)
N 19,055 22,948 23,206 27,817
Hypertension –0.3727(0.3246)
–0.7706(6.3744)
–0.5395 * (0.3236)
0.3257 ** (0.1358)
–0.5698 **(0.2812)
0.4159 ***(0.1297)
N 20,282 24,712 24,741 29,985
Dental Loss –0.3290 *** (0.1203)
–0.2842 ***(0.1011)
–0.4126 **(0.1877)
–0.0027 (0.1432)
–0.5484(0.5424)
-
Include dental care affordability –0.3820 *** (0.1398)
–0.3240 ***(0.1174)
–0.4231(0.2724)
–0.0644 (0.5319)
0.5450 ** (0.2531)
0.0290 (0.1245)
Include dental care affordability and utilization
–0.3716 *** (0.1314)
–0.3206 ***(0.1126)
–0.4072 * (0.2218)
–0.0872 (0.3390)
–1.3677(1.5992)
0.3630 (0.6865)
Include dental care affordability and exogenous veteran
–0.3716 *** (0.1314)
–0.3206 ***(0.1126)
–0.4300 **(0.1833)
–0.0231 (0.0153)
–0.5516 **(0.2693)
–0.0246 (0.0171)
N 16,686 20,352 20,373 24,695Notes: See notes in Table 1. Diabetes is whether one was diagnosed for diabetes or board-line diabetes. Insulin-independent (dependant) is whether one was (not) taking insulin on a regular basis. Hypertension is whether one was told by a doctor that he/she had hypertension on at least two different visits. Dental loss is whether one lost all permanent teeth. Dental care affordability is whether one needed dental care but could not afford it in the past 12 month. Dental service utilization is whether one never saw a dentist of all kinds.
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Table 9: Heterogeneity of Education Effect on Obesity and Its Co-Morbidities
White NV NV White All Obesity Diabetes Obesity Diabetes Obesity Diabetes Obesity Diabetes
College degree and above –0.6055 **(0.2711)
–0.1775 * (0.1060)
–0.4386 **(0.2087)
–0.1940 * (0.1189)
–0.6089 **(0.2973)
–0.3225 *(0.1803)
–0.5058 **(0.2406)
–0.5284 **(0.2440)
Associated degree and above –0.8765 *(0.4489)
–0.2271 * (0.1390)
–0.5359 **(0.2520)
–0.1950 (0.1217)
–0.9365 (0.5734)
–0.2291 (0.1815)
–0.6418 **(0.3239)
–0.5602 *(0.3102)
College enrollment –1.6379 (1.0538)
–0.3652 * (0.2001)
–0.7901 (0.4884)
–0.1144 (0.1722)
–0.5378 (0.3877)
–0.4222 (0.2723)
–0.3610 (0.3804)
–0.2387 (0.1866)
Years of schooling beyond H.S. –0.1821 *(0.0972)
–0.0534 * (0.0312)
–0.1337 *(0.0703)
–0.0476 * (0.0258)
–0.0957 (0.0716)
–0.0571 (0.0395)
–0.0878 (0.0577)
–0.0996 **(0.0484)
Years of schooling beyond 11th grade –0.1819 *(0.0958)
–0.0537 * (0.0301)
–0.1241 *(0.0680)
–0.0459 * (0.0246)
–0.0985 (0.0726)
–0.0565 (0.0385)
–0.0773 (0.0535)
–0.1031 **(0.0506)
Years of schooling –0.1076 (0.1284)
–0.0490 (0.0308)
–0.0599 (0.0513)
–0.0231 (0.0218)
–0.0328 (0.0615)
–0.0463 (0.0362)
–0.0323 (0.0453)
–0.0831 (0.0615)
Dental L. Hypert. Hypert Dental L. Hypert Dental L. Hypert Dental L.
College degree and above –0.3727 (0.3246)
–0.3820 ***(0.1381)
–0.4719 (0.5149)
–0.3240 *** (0.1174)
–0.5395 *(0.3236)
–0.4231 (0.2724)
–0.5698 **(0.2812)
–0.5450 **(0.2531)
Associated degree and above –0.3299 (0.3186)
–0.4159 ***(0.1511)
–0.3014 (0.3313)
–0.3370 *** (0.1374)
–0.4846 (0.3578)
–0.4401 **(0.1915)
–0.6607 **(0.3066)
–1.0178 (0.9169)
College enrollment –0.3382 (0.4070)
–0.4427 ***(0.2185)
– –0.2650 (0.1898)
–0.4760 (0.3390)
–6.6541 (43.9603)
–0.3789 (0.2913)
–0.3018 *(0.1683)
Years of schooling beyond H.S. –0.0966 (0.0785)
–0.0838 ***(0.0318)
–0.1301 (0.1057)
–0.0726 ** (0.0307)
–0.1302 *(0.0786)
–0.0827 **(0.0400)
–0.1458 *(0.0665)
–0.2148 (0.1732)
Years of schooling beyond 11th grade –0.0983 (0.0774)
–0.0772 ***(0.0297)
–0.1177 (0.0905)
–0.0653 ** (0.0278)
–0.1191 *(0.0721)
–0.0767 **(0.0368)
–0.1389 *(0.0631)
–0.1480 (0.0946)
Years of schooling –0.0988 (0.0836)
–0.0715 ***(0.0291)
–0.1098 (0.0996)
–0.0675 ** (0.0257)
–0.1059 (0.0676)
–0.0713 **(0.0334)
–0.0934 (0.0591)
–0.0933 **(0.0471)
Notes: See notes in Table 1 and 9 ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.
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Figure 1: Number of Induction (top) and Fraction of Veterans (bottom)
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Figure 2a: College Graduation Rate of U.S.-Born Non-Veteran Males and Females and Their Difference (Data Source: NHIS 1998–2003)
Figure 2b: Obesity Rate of U.S.-Born Non-Veteran Males and Females and Their Difference (Data Source: NHIS 1998–2003)
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Figure 3a: College Graduation Rate of U.S.-Born Non-Veteran White Males and Females and Their Difference (Data Source: NHIS 1998–2003)
Figure 3b: Obesity Rate of U.S.-Born Non-Veteran White Males and Females and Their Difference (Data Source: NHIS 1998–2003)
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Figure 4: Gender-Difference and Control-Treatment Gender-Difference in Schooling CDF (Top: Non-Veterans; Bottom: All Individuals)
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Figure 5: Gender-Difference and Control-Treatment Gender-Difference in Schooling CDF (Top: White Non-Veterans; Bottom: All White Individuals)
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