Drawn into violence: evidence on "what makes a criminal" from the Vietnam draft lotteries.
Lindo, Jason M. ; Stoecker, Charles
I. INTRODUCTION
"CRIMINALS ARE MADE, NOT BORN."
--Stenciled sign left behind by Michigan school board member and
suicidal mass murderer Andrew Kehoe after killing 45 people, mostly
school children.
Understanding the extent to which criminals are "made"
and, further, identifying the determinants of criminal behavior is of
utmost importance to any society that wants to reduce crime. To date,
most research in this area has focused on the causal effects of
individuals' immediate environments. (1) Quasi-experimental studies
that explore how individuals' backgrounds affect criminal behavior
are more rare with a handful of studies on neighborhoods (Oreopoulos
2003), education (Lochner and Moretti 2004), foster care (Doyle 2008),
peers (Bayer, Hjalmarsson, and Pozen 2009), and beauty (Mocan and Tekin
2010) providing notable exceptions. In this paper, we add to this strand
of the literature by exploiting the randomness of the national Vietnam
draft lotteries to examine the effects of military service on subsequent
incarceration.
Our study also has implications for the military and for the
treatment of veterans. First, this paper can be thought of as exploring
a potentially important long-term cost of military engagements that
might be important for comprehensive cost-benefit considerations.
Second, our results speak to what types of special accommodations might
be reasonably made for those who have served in the military. This is an
issue that has been taken quite seriously in the criminal justice
system, as special courts that focus on rehabilitation have been set up
to try cases involving nonviolent veteran offenders. Further, the
results of our analysis can inform the extent to which resources ought
to be allocated toward the treatment of veterans who might exhibit signs
of instability.
While we consider the impacts of military service on multiple types
of crimes, our primary focus is on violent crimes. Although this would
be a natural choice for any study considering the effects of military
service on crime since the military trains soldiers to engage in
violence, the Vietnam Era provides an especially interesting context.
Notably, the Vietnam Era coincided with an important shift in military
training motivated by S.LA. Marshall's pioneering research
documenting extremely low firing rates for U.S, soldiers serving in
World War II. In order to overcome soldiers' reluctance to fire at
enemy combatants, in the late 1960s the military began making conscious
efforts to provide more realistic training scenarios (Grossman 2009).
(2) While this desensitization to engaging in violence may be crucial to
survival in a combat zone, it is easy to see how it might lead to
problems after a soldier returns to civilian life. (3)
Of course, there are several other possible mechanisms through
which military service might affect crime. Engagements with real-enemy
combatants in the combat zone have been shown to have impacts over and
above the effects of being in the military (Cesur, Sabia, and Tekin
2011; Galiani, Rossi, and Schargrodsky 2011; Rohlfs 2010). In addition,
military service may increase crime because it precludes labor market
experience and thus reduces wages (Angrist 1990; Abadie 2002; Angst and
Chen 2011; Imbens and van der Klaauw 1995; Siminski and Ville 2011a,
2011b) or because of possible effects on opiate use (Robins, Davis, and
Goodwin 1974). On the other hand, the discipline imparted by the
military environment may make individuals less likely to commit crimes.
(4) Further, military service could reduce criminality via an
incapacitation effect, as individuals are in the military environment at
the ages at which they are at highest risk of incarceration.
A sizable literature links military service to criminal behavior,
particularly to violent behavior, but much of the prior work on this
topic lacks plausibly exogenous variation and focuses on small
non-random samples. Exogenous variation in military service is crucial
since men who are more likely to engage in criminal activities may be
disproportionately likely to enlist. Galiani, Rossi, and Schargrodsky
(2011) overcome this selection bias using variation driven by
Argentina's draft lotteries. Relative to our study, this earlier
work has the advantage of being able to explore cohorts serving the
Malvinas War and others serving during peacetime. However, it is
somewhat limited in its ability to measure impacts by type of crime,
which can only be identified for those going through the criminal
justice system approximately 20-30 years after service. Our results
suggest that this limitation is not trivial, as we find offsetting
effects on incarceration for violent and nonviolent crimes 7 to 9 years
after conscription. (5)
In this paper, we also use variation provided by draft lotteries
but focus on the U.S. context. In particular, our identifying variation
is driven by: (1) the Vietnam Era draft lotteries which randomly
assigned lottery numbers to exact dates of birth and (2) the fact that
the military drafted men, starting with the lowest lottery numbers,
until manpower requirements were met each year. Utilizing this exogenous
variation in draft status, we are able to determine the extent to which
military service affects criminal behavior by comparing the probability
of incarceration (based on the number of births) for those whose lottery
numbers were called to report for induction into the military to the
incarceration rates for those whose numbers were not called. We do this
by combining data from the 1979, 1986, and 1991 Surveys of Inmates in
State and Federal Correctional Facilities (SISFCF) with data from the
Vital Statistics of the United States (VSUS) to create measures of
incarceration probabilities for each day of birth for the cohorts
affected by the draft lotteries. We supplement this analysis with data
on prison admissions from 1983-1991 via the National Corrections
Reporting Program (NCRP).
While these inmate data are well-suited to identifying the effect
of draft eligibility, they are not well-suited to directly estimating
the effect of military service. In particular, it would be inappropriate
to estimate the first-stage effect of draft eligibility on military
service using an endogenously selected subsample of individuals exposed
to the draft, such as a sample of inmates. For this reason, we obtain
first-stage estimates for the overall population using restricted U.S.
Census data from 2000. Combining the estimates from each of these
sources, we obtain two-sample instrumental-variable estimates of the
effect of military service on incarceration. We discuss potential
threats to the validity of this approach in Section IV.
We find evidence of positive impacts on incarceration for violent
crimes among whites and offsetting impacts of a similar magnitude on
incarceration for nonviolent crimes. This is particularly evident in
1979, where two-sample instrumental variable estimates indicate that
military service increases the probability of incarceration for a
violent crime by 0.34 percentage points and decreases the probability of
incarceration for a nonviolent crime by 0.30 percentage points. We find
less convincing evidence of impacts on nonwhites for whom the estimates
are imprecise, but we also cannot rule out that these effects are large.
The rest of the paper is organized as follows. Section II provides
background on the Vietnam Era draft lotteries. Sections 1]I and IV
describe our data and empirical strategy. Section V presents our results
and robustness checks. Section VI discusses our results and concludes.
II. BACKGROUND ON THE DRAFT LOTTERIES
In an attempt to fairly allocate military service in Vietnam, a
total of seven national lottery drawings were held to determine who
would serve in the military--although conscription was halted after the
third lottery. The three lotteries used to draft servicemen were held in
1969, 1970, and 1971. While the 1969 lottery applied to those born
1944-1950, each subsequent drawing applied only to men who turned 18 in
the year of the lottery. In particular, the 1970 lottery applied to
those born in 1951 and the 1971 lottery applied to those born in 1952.
In each drawing, the birthdays of the year were randomly assigned a
Random Sequence Number (RSN). In the 1969 drawing September 1st was
assigned RSN 1 so men born on September 1st were asked to report to
their local draft boards for potential induction before men born on
other days. April 24th was assigned RSN 2 so men born on that day were
asked to report second, and so forth. The military continued to call men
for potential induction in order of RSN until the manpower requirements
were met for that year. The last RSN called for service, also known as
the highest Administrative Processing Number (APN), was 195 for the 1969
drawing, 125 for the 1970 drawing, and 95 for the 1971 drawing.
Throughout the paper, we refer to individuals with RSNs less than or
equal to the APN as "draft eligible."
While the issue was addressed for later drawings, there was a
noteworthy mechanical problem with the randomization mechanism used in
the 1969 drawing. In particular, each birthday was coded onto a capsule
and these capsules were added month by month into a drawer, with the
drawer being "shuffled" after each month. As a result of
incomplete mixing, dates later in the year remained on top of the pile
and were more likely to be drawn first and thus called first for
induction (Fienberg 1971). This phenomenon is shown in Figure A 1 in the
Appendix, which plots the number of draft eligible days by month for
each lottery. To the extent to which people born in later months might
be more or less likely to commit crimes, this could lead to omitted
variable bias. We follow the previous literature and address this
potential issue by controlling for year-by-month-of-birth fixed effects
in our analysis (Angrist and Chen 2011; Angrist, Chen, and Frandsen
2010; Conley and Heerwig 2009; Eisenberg and Rowe 2009). (6)
For multiple reasons, military service is not perfectly predicted
by being born on a draft-eligible day. Men born on non-eligible
birthdays could volunteer and men born on eligible days could fail the
medical exams, refuse to report, or apply for various exemptions.
Despite these issues, the draft had a significant effect on military
service, the magnitude of which is discussed in Section V.A.
III. DATA DESCRIPTION AND CONSTRUCTION
Our primary analysis uses data on incarceration from the 1979,
1986, and 1991 SISFCF, which are representative of the prison population
in state and federal correctional facilities. Although it would be
desirable to use the 1974 survey to consider potential incapacitation
effects, exact dates of birth are not available for this survey year. In
addition to exact dates of birth, the survey waves we use contain
information on each prisoner's race, sex, and the type of offense
for which he was incarcerated. The type of offense is classified
according to approximately 80 offense codes and each inmate is
associated with up to four different offense codes (since inmates can
concurrently serve time for multiple offenses). We define a prisoner as
incarcerated for a violent crime if any of the listed offenses involve
violence and as incarcerated for a nonviolent crime if none of the
listed offenses involve violence.
The 1979, 1986, and 1991 waves of the SISFCF used in this analysis
contain information on 6642, 6612, and 6631 male inmates subjected to
the drafts, respectively. In selecting an appropriate sample to analyze,
there is a tradeoff between ease of interpretation of the results and
sample size. The most-straightforward results to interpret are those
where data are limited to a single survey wave. For example, if we limit
the sample to cells collapsed from the 1979 data, the estimates will
provide the estimated effect of military service on the probability of
being incarcerated 7 to 9 years after conscription. The interpretation
is more complicated when we expand the sample to include all three
survey waves, where we are estimating a combination of the probabilities
of being observed in prison 7-9, 14-16, and 19-21 years later. On the
other hand, pooling survey years can improve precision. For this reason,
we present estimates that utilize all of the available data and
estimates stratified on survey years.
Limiting the sample to males, we conduct the analysis separately
for whites and nonwhites at the date of birth by survey year level. Each
observation represents a collapsed cell measuring the probability of
incarceration in survey year s for individuals born on day ymd. To
construct this variable, we divide the number of male convicts we
observe in prison in survey year s with date of birth ymd, calculated
using the SISFCF's sampling weights, by the number of males that
were born in the United States on day ymd:
(1) Incarceration[Probability.sub.symd] = #of
[Inmates.sub.symd]/#of [Births.sub.ymd].
The denominator for the equation above comes from the VSUS which
reports births by race, gender, and month. Since the VSUS only reports
births by month prior to 1969, we construct the number of births for
each given day. We report results in which the number of births in each
month are apportioned evenly across the days in the month. The results
are nearly identical using strategies for constructing the denominator
that adjust for differing birth patterns observed on weekdays versus
weekends, These robustness checks are described further in the Appendix.
The data used to estimate the first-stage effect of draft
eligibility on military service are from the 2000 Census long-form
sample, which includes approximately one-sixth of U.S. households. For
more details on these data, see Angrist and Chen (2011) whose sample is
identical.
To properly link each birthday with a particular draft lottery
number we use the draft lottery information available from the Selective
Service System. This allows us to associate each birth date with a
lottery number for each of the lotteries.
IV. EMPIRICAL STRATEGY
Broadly speaking, regressions of social outcomes on veteran status
are unlikely to yield unbiased estimates of the effects of military
service because military service is not random. With respect to crime,
this approach will yield positively biased estimates if aggressive
individuals are both more likely to serve in the military and to commit
crimes. Alternatively, if individuals with more respect for authority
are more likely to become veterans and less likely to commit crimes then
the estimated effect would be negatively biased.
Out of concern for such sources of selection bias, we consider
variation in military service across dates of birth generated by the
Vietnam draft lotteries. We begin by estimating:
(2) Incarceration[Probability.sub.symd] = [phi] + [gamma] *
Draft[Eligible.sub.ymd] + [[chi].sub.ym] + [[epsilon].sub.symd]
where Draft[Eligible.sub.ymd] is an indicator variable that equals
one if men born on date ymd are assigned a lottery number that makes
them eligible to be drafted into the military and zero otherwise, while
[[chi].sub.ym] are year-of-birth-by-month-of-birth fixed effects
(included to address mechanical problems associated with the draft
lottery that we described above). The parameter [gamma] is the average
reduced-form effect of draft eligibility on the probability of
incarceration. Because the data span multiple survey years, we also
include survey,-year fixed effects as controls where applicable. (7)
If all men whose birthday was drawn in the lottery served in the
military (i.e., no exceptions made) and no men whose birthday was not
drawn in the lottery served in the military (i.e., no volunteers),
[gamma] would also reflect the impact of military service. Because
exceptions were made and there were volunteers, the estimate must be
scaled up by the (inverse of the) effect of draft eligibility on
military service, which can be estimated by:
(3) Veteran[Probability.sub.ymd] = [eta] + [beta] *
Draft[Eligible.sub.ymd] + [[psi].sub.ym] + [[omega].sub.ymd].
Because an unbiased estimate of [beta] requires data on a random
sample of the population, as opposed to an endogenously-selected
subsampie of inmates, we estimate the person-level analogue of Equation
(3) using restricted-use U.S. Census data from 2000. (8) We then obtain
the two-sample instrumental-variable estimate of the effect of military
service by taking the ratio of the reduced-form estimate and the
first-stage estimate,
(4) [MATHEMATICAL EXPRESSION NOT REPRODUCIBLE IN ASCII],
and estimate its standard error using the delta method. (9) The
standard-error estimates for the first-stage and reduced-form estimates
used in this calculation are clustered on lottery numbers to address the
fact that the former is based on individual-level data while the latter
is based on data aggregated to the birth-date level.
While random assignment ensures that [??] will be unbiased, the
instrumental variables estimation strategy relies on the assumption that
veteran status is the only mechanism of transmission between draft
eligibility and the probability of incarceration. We acknowledge that
[??] will be biased if draft eligibility also affects incarceration
probabilities through other mechanisms. It has been documented that
eligibility had a positive impact on educational attainment (Angrist and
Krueger 1992; Angrist and Chen 2011; Card and Lemieux 2001). (10) To the
extent that increased education levels lead to decreased crime (Lochner
and Moretti 2004) the extra education conferred by draft eligibility
should bias our estimates of a downward. Another potential issue is that
military service might affect incarceration through its impacts on
mortality; however, researchers have found little evidence that military
service affects health (Conley and Heerwig 2009; Dobkin and Shabani
2009; Siminski and Ville 2011a, 2011b), which might be explained by the
generous health benefits that tend to be provided to veterans. (11) In
addition, the fact that our data exclude those serving in military
prisons may cause us to understate the effect of military service on
criminal behavior. In addition, we acknowledge that impacts on crime may
diverge from impacts on incarceration if military service affects the
probability of getting caught conditional on committing a crime or if
veterans receive differential treatment from law enforcement officers or
judges. We should also note that this instrumental variable approach
identifies the local average treatment effect (LATE), or the effect of
military service on those individuals who can be compelled to enter the
military by the draft lotteries.
V. RESULTS
This section is organized into multiple parts. We begin by
presenting estimates of the first-stage effect of draft eligibility on
military service. Next, we show summary statistics for incarceration
probabilities. We then present our main results, which are followed by
robustness checks to verify that these results are not driven by the
particular birthdays that were drawn in any given lottery or by
avoidance behaviors among eligible men. Finally, we conduct a
supplementary analysis using prison-admissions data from 1983 to 1991.
A. First-Stage Effect of Eligibility on Military Service
As described above, an unbiased estimate of the effect of the
Vietnam draft lotteries on military service requires a random sample of
individuals exposed to the draft. We obtain these estimates using
restricted-use U.S. Census data from 2000. (12)
Table 1 shows how draft eligibility affected military service for
the 1944-1952 cohorts. As demonstrated in earlier studies, draft
eligibility did not have a significant impact on the earliest of these
cohorts subject to the national lottery--this is not surprising because
a large share of the capable men in these cohorts were already called to
serve via local drafts. In subsequent sections, we follow the existing
literature and focus on the 1948-1952 cohorts, for whom the first-stage
estimate is clearly strong for both whites and nonwhites. For these
cohorts, eligibility increased the probability of military service by
approximately 11 percentage points for whites and 7 percentage points
for nonwhites, on average, with especially large impacts for those born
1950-1952.
B. Summary Statistics
Table 2 presents incarceration probabilities by survey wave, race,
and draft eligibility status. The table separately considers
incarceration for all crimes, violent crimes, drug-related crimes,
property crimes, and public order crimes. (13) These categories are
mutually exclusive, but since an inmate can be concurrently serving time
for multiple offenses, he may contribute to multiple lines in the table.
In most cases, the statistics in Table 2 suggest that induction had no
significant effects. On the other hand, they suggest that induction
increased incarceration for violent crimes among whites by approximately
15%. This is most apparent in 1979 incarceration rates, as is an
offsetting decrease in nonviolent crimes for whites. There is also
evidence that eligibility increased nonwhite incarceration for violent
and property crimes in the 1991 survey wave. Nonetheless, because of the
mechanical complications with the first national draft lottery, we do
not expect these estimates to be free of bias.
C. Main Results
Table 3 reports the estimated effects of draft eligibility and
military service on incarceration probabilities among whites, with
separate panels for violent crimes, nonviolent crimes, and all crimes.
The data are aggregated to the exact date of birth by survey year level.
The estimates control for month-by-year-of-birth fixed effects to deal
with the fact that later birth months had a higher probability of being
drawn in the 1969 draft due to mechanical problems with the lottery
board's randomization method.
Column 1 shows estimates that pool data from the three survey years
while also controlling for survey-year fixed effects. These estimates
echo the results presented in the previous section. The estimated impact
on incarceration for a violent crime is significant at the 10% level,
indicating that eligibility increased the probability of incarceration
by approximately 0.03 percentage points. The corresponding two-sample
instrumental-variables estimate indicates that Vietnam Era military
service increased the probability of incarceration for a violent crime
by 0.27 percentage points. In contrast, these data indicate a negative
effect on incarceration for a nonviolent crime, although this estimate
is not close to being statistically significant at any conventional
level. That said, because of this offsetting impact, the estimated
effect on the probability of incarceration for any crime (Panel C,
Column 1) is close to zero.
Columns 2 through 4 stratify on the three survey years, with the
most precise estimates using data from 1979 and the least precise
estimates using data from 1991. (14) To put these results into context,
it is important to keep in mind that the men conscripted by the
lotteries would have finished their mandatory service 5 to 7 years
before the 1979 survey was conducted.
The estimates using data from 1979 (Column 2) are qualitatively
similar but stronger than the estimates that pool together the three
survey years. The estimated impact of Vietnam Era military service on
incarceration for a violent crime is 0.34 percentage points and
significant at the 5% level. The estimated impact on incarceration for a
nonviolent crime is of a similar magnitude (-0.30 percentage points) and
significant at the 10% level. Not surprisingly then, the estimated
impact on incarceration for any crime is close to zero. (15)
The estimates using data from 1986 are qualitatively similar but do
differ in important ways. In particular, the estimated impact on
incarceration for a violent crime is smaller in magnitude (0.15
percentage points) and the estimated impact on incarceration for a
nonviolent crime is larger in magnitude (-0.47 percentage points).
However, these estimates are not close to being statistically
distinguishable from those focusing on incarceration in 1979.
The estimates using data from 1991 suggest a positive effect on
incarceration for violent crimes and no effect on incarceration for
nonviolent crimes. That said, these estimates are the least precise
among those shown in Table 3, with standard-error estimates two- to
three-times larger than similar estimates using data from 1979.
Table 4 presents estimates for nonwhite men. These estimates
suggest there is no effect of Vietnam Era service on incarceration for
violent crimes in 1979 or 1986 but, curiously, indicate a large effect
in 1991. These estimates suggest that there was either a large delayed
impact on nonwhite males that manifested in the late 1980s or that the
1991 estimate is a statistical artifact. The results in Section V.F,
where we estimate impacts on prison admissions from 1983 to 1991,
suggest that the latter explanation is most likely.
The estimated effects on nonwhite incarceration for nonviolent
crimes are never statistically significant and, like the estimated
effects on incarceration for violent crimes, vary in sign. That said, it
is important to note that the first stage is relatively small for
nonwhites and the confidence intervals are quite large. As such, we
generally cannot rule out large effects. For example, the standard-error
estimate for the impact on nonwhite violent crime incarceration rates in
1979 is so large that it includes an effect four times the magnitude of
the estimated effect for whites.
Precisely identified effects, both good and bad, for whites but
imprecise effects for nonwhites is a common feature among studies that
use the Vietnam draft as an instrument for military service. Military
service in the Vietnam Era has been shown to depress wages (Angrist
1990), increase transfer income (Angrist, Chen, and Frandsen 2010), and
increase GI bill-related education (Angrist and Chen 2011) for whites
but the estimated effects for nonwhites have been inconclusive.
D. Estimates Using More-Narrow Crime Categories
In order to shed light on our main results, Tables 5 and 6 show the
effect of draft eligibility on subcategories of violent, property, and
drug-related crimes. Because incarceration probabilities are small for
these narrowly defined categories, these tables report estimated effects
per 10,000 instead of per person. These estimates should be interpreted
with caution because the sample size of inmates contributing to each
estimate is relatively small when the data have been disaggregated in
this fashion. As a result, the estimates rarely rise to the level of
statistical significance and often change signs when considering data
from different survey years.
The estimates that are relatively robust for whites (Table 5)
suggest that the overall impact on violent crime among whites is driven
by incarcerations for murder, robbery, and kidnapping offenses. In
contrast, the estimated impacts on nonviolent crime categories are not
sufficiently robust to yield insight into our earlier results. The
estimates for nonwhites (Table 6) demonstrate that the estimated impact
on violent crime in 1991 among nonwhites is driven by robberies. More
broadly, the estimated effects on these narrow categories of crime are
not robust across survey years for nonwhites, with the exception of
burglary for which we sometimes see significantly elevated rates among
the draft-eligible population.
E. Robustness Checks Using Lotteries for Unaffected Cohorts
In this section, we conduct two falsification tests, similar in
spirit to those in Galiani, Rossi, and Schargrodsky (2011), in order to
address potential concerns regarding the use of the lottery for
identification.
One possible concern with our main estimation strategy is that,
despite being random, the first numbers drawn (which led to eligibility)
may have included a disproportionate number of birth dates that we would
expect to be associated with higher rates of crime even if no one was
called to serve in the military. For example, this could occur if men
born on dates with the earliest lottery numbers disproportionately came
from disadvantaged backgrounds.
To verify that this type of phenomenon is not driving our results,
we apply each of the three lotteries to cohorts that the given lottery
did not affect and conduct the analysis as before. For example, we test
the 1969 draft that applied to the 1944-1950 cohorts by matching the
1969 lottery numbers to the birth dates in the 1941-1942 and 1951-1959
cohorts and testing for effects. Since the 1969 lottery did not actually
apply to these cohorts, we should not find significant effects unless
the 1969 lottery suffered from the potential problem described above. We
test each lottery using all of the unaffected cohorts that our data sets
allow us to cover, ranging from 1942 to 1959. (16)
The results of this falsification exercise, by race and crime type,
are presented in Table 7. Consistent with random assignment, the
estimates are neither uniformly positive nor uniformly negative.
Further, just two of the 48 "placebo tests" are significant at
the 10% level.
A second possible concern with our empirical strategy relates to
the validity of the exclusion restriction for the two-sample
instrumental-variable estimates. In particular, one might be concerned
that draft-eligible men may have engaged in draft-avoidance behaviors
that could affect their probability of incarceration. (17) Using
hypothetical APNs taken from the 1969, 1970, and 1971 drawings, we test
for this possibility by considering possible effects on men who were
assigned low draft lottery numbers in the four non-binding lotteries
that took place in 1972-1975. Since these lottery numbers were assigned
but their results were not used to induct men into the military, we
expect to see no link between low lottery numbers and violent crime
unless lottery numbers affected criminality through mechanisms besides
military service. Table 8 shows these results by race and crime type.
Again, the results are not consistently positive or negative and just
two of 48 are statistically significant at the 10% level. (18)
F. Analysis of Prison Admissions Data, 1983-1991
In this section, we use data from the NCRP to further investigate
some of the results presented in prior sections. These data are
attractive because they provide information on all prisoners admitted to
state correctional facilities on an annual basis but are limited because
they are only available beginning in 1983, 11-13 years after most
draftees completed service. Although these data track all movements
across prisons, we focus on admissions that are due to court commitments
to reduce the likelihood of "double counting" prisoners. As in
previous sections, we combine these data with vital statistics data,
which are used for the denominator of the outcome variable. However,
here we use the number of number of individuals admitted per 10,000
births at the exact date of birth level since the number of inmates
admitted into prison per year is relatively small.
Panels A and B of Table 9 show no systematic evidence that draft
eligibility is related to new admissions of white prisoners in the
mid-1980s to early 1990s, for violent or nonviolent crimes. These
results are consistent with our earlier results, which demonstrated that
the effects for whites manifested soon after the war ended, that is,
before the time period spanned by these admissions data. (19)
Panels C and D focus on admissions of nonwhite prisoners. Recall
that our analysis of nonwhite incarceration rates revealed no
significant effects in 1979 or 1986 but did suggest that there was an
effect on incarceration rates for violent crimes in 1991. Taken at face
value, this suggests that we should see a significant effect on
admissions for violent crimes from the mid-1980s to the early-1990s.
However, the estimates shown in Panel C do not reveal any such effect.
This suggests that the significant estimate for nonwhite incarceration
for violent crimes in 1991 is likely a statistical artifact. Further
corroborating this interpretation, we also find no evidence of an effect
on admissions for robberies, the category that drove the significant
estimate in the 1991 prisoner data.
VI. DISCUSSION AND CONCLUSION
Our results highlight the importance of one's background on
criminal behavior. We find that military service increases the
probability of incarceration for violent crimes among whites, with point
estimates suggesting an impact of 0.27 percentage points. To put this
magnitude into context, it is approximately 12 times the estimated
effect of a 1-year reduction in education (Lochner and Morreti 2004). If
we were to extrapolate from our results to the broader set of 7,2
million white Vietnam-Era veterans, it would suggest that military
service contributed to an additional 28,300 men being incarcerated for a
violent crime in 1979. (20)
Putting aside differences between the United States and Argentina,
these results may initially seem to be at odds with Galiani, Rossi, and
Schargrodsky (2011) who also exploit a draft lottery but do not find any
evidence that military service affects violent crime. However, our
analysis suggests that the effects on violent crime manifest soon after
military service is complete, as they are present in 1979 for cohorts
who served in the early 1970s. This is critical, as Galiani, Rossi, and
Schargrodsky (2011) would be unable to detect such effects in their
analysis that identifies the 1958-1962 cohorts going through the
criminal justice system from 2000 to 2005.
We also note that our results are in contrast to Rohlfs (2010) who
finds significant effects of combat exposure on sell-reported violence
among nonwhites and imprecise estimates for whites. Though this
difference could be because combat exposure and military service more
broadly defined have different effects, it could also be due to
differences in power. In particular, Rohlf's cohort-based
instrument for combat exposure (military deaths in Vietnam) is a
stronger predictor of combat exposure for nonwhites than whites whereas
our instrument (draft eligibility) is a stronger predictor of military
service for whites than nonwhites.
We also find evidence of offsetting impacts on incarceration for
nonviolent crimes among whites. This suggests that military service may
not change an individual's propensity to commit crime but instead
may cause them to commit more-severe crimes involving violence. (21)
Our identification strategy only allows us to estimate the effects
of military service on conscripts during the Vietnam Era, and as such,
should be extrapolated to the modern setting with caution. Many features
of warfare have changed since the Vietnam Era. However, multiple
features of today's military suggest that our results may be, at
least partially, relevant today. The military has continued and
escalated the use of highly realistic training simulations, a legacy of
late 1960s efforts to desensitize soldiers to engaging with enemy
combatants. For example, the military currently uses Iraqi nationals as
role-players in training exercises in order to help cadets "put a
human face and picture on Iraqi society." (22) In addition, the
rates of post-traumatic stress disorder for veterans of Iraq and
Afghanistan (14%-25%) are quite similar to the rates for those who
served in the Vietnam War (18%-20%), though these could be artificially
equalized by a change in the likelihood of diagnosis. (23)
Furthermore, today's military readily acknowledges that
soldiers often struggle with the transition to civilian life and that
skills that promote success in combat can translate into unhealthy
behaviors at home. For this reason, each branch of the military has
programs to help ease the transition. Although research highlights some
promising results for the average soldier (Adler et al. 2009; Castro et
al. 2006), recent evidence raises serious concerns about the treatment
of servicemen with the most-severe mental problems (Stahl 2009). (24)
Coupled with this mixed evidence on the efficacy of the treatment
provided to soldiers at risk of mental-health problems, our results,
which demonstrate grave consequences of military service, highlight the
need for further research in this area.
Finally, our results have important implications for the legal
system, which has 23 recently established pilot courts that try only
cases in which the offender is a veteran. (25) Possibly out of some
sense of society's responsibility for their behavior, these courts
focus on rehabilitation and treatment programs instead of incarceration.
In 2008, senators Kerry and Murkowski introduced legislation to extend
the program nationally. The existence of this special court system
implicitly creates a separate legal class for veterans and tacitly
acknowledges that military service can have negative consequences that
manifest in criminal behavior once servicemen return home. But these
courts exclude the violent offenders. Our analysis suggests that these
are the offenses for which military service is most clearly responsible.
ABBREVIATIONS
APN: Administrative Processing Number
LATE: Local Average Treatment Effect
NCRP: National Corrections Reporting Program
RSN: Random Sequence Number
SISFCF: Surveys of Inmates in State and Federal Correctional
Facilities
VSUS: Vital Statistics of the United States
doi: 10.1111/ecin.12001
Online Early publication March 24, 2013
APPENDIX A
[FIGURE A1 OMITTED]
APPENDIX B: ALTERNATIVE STRATEGIES FOR CALCULATING BIRTHS PER DAY
As we describe in the main text, in order to calculate
incarceration rates for exact dates of birth, we must construct the
number of births per day based on the VSUS, which only reports births
per month for the cohorts we consider. The results we show throughout
the paper apportion the number of births in each month evenly across the
days in each month. In this section, we describe two alternative
strategies that give nearly identical results. The first alternative
that we have considered accounts for differing birth patterns across
weekdays and weekends. It has been documented that in recent periods
more cesarean sections and birth inductions take place on each weekday
than on each weekend day (Dickert-Conlin and Chandra 1999), possibly
because doctors want to schedule these procedures on days when the
hospital is more heavily staffed. To account for this weekday-weekend
variation, we match each day of the week in the data for our cohorts of
interest to the same day of the week in the 1969 data for which we have
daily birth counts. The percentage of births in the month that occurred
On that day in the later data is used to apportion the total monthly
births in the earlier data across days. Consider January 1st, 1950 which
was a Sunday: The first Sunday in 1969 was January 5th. In 1969, 2.7% of
January births occurred on the first Sunday. So 2.7% of the births in
January 1950 are assigned to January 1st, 1950. This procedure is
repeated for each day and the percentages of birth in each month are
normalized to 100. For some years the days in the first or last week of
the year are matched forward or backward to find a match. For instance,
in 1944 the 53rd week contains a Friday, Saturday, and Sunday. In 1969,
the 53rd week only contains a Tuesday and a Wednesday. So for 1944 the
last 3 days are assigned the birth percentages on Friday, Saturday, and
Sunday that occurred in the 52nd week instead of the 53rd. Another
alternative strategy we have considered recognizes that birth technology
has changed over the 25 years that elapse between the first year of
interest and 1969 (the first year for which we have births at the day
level, as used in the first alternative strategy above). We can obtain
an estimate of the weekend effect that uses only data from the period of
interest by exploiting the different number of weekend days that fall on
a given month across years. We estimate:
(A1) [Births.sub.ym] = [alpha] + [beta] * Weekend[Days.sub.ym] +
[v.sub.y] - [[delta].sub.m] + [[epsilon].sub.ym].
This is a regression of the number of births in each month-year on
the number of Saturdays and Sundays in the month with fixed effects for
month and year. The coefficient [beta] gives the decrease in the number
of births when a month has one additional weekend day. January 1948 had
one more Sunday than January 1947. The number of white births in January
1948 was less than the number of white births in January 1947. Some of
the decrease in the number of births in January 1948 was due to the
weekend effect. Since January had 31 days in both years, some of the
decrease in births was due to births being shifted from the extra
weekend day at the end of the month into February. The number of births
in each month are then apportioned out where each weekend day gets a
fewer number of births than each weekday. All weekdays are treated alike
and all weekend days are treated alike. The advantage of this strategy
is that it does not impose the weekend effect from a later era on the
monthly birth data from 25 years earlier. We have also explored a
variation of this strategy where the weekend effect is a percentage
change in the total monthly births rather than a fixed decrease in the
number of births. These strategies likely improve the accuracy of our
measures of births per day and, hence, the accuracy of our measures of
incarceration rates. However, because they do not change the results, we
adopt the simpler and more transparent method described in the main
text.
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JASON M. UNDO AND CHARLES STOECKER *
* We thank the Co-Editor, Darren Lubotsky, and two anonymous
referees for thoughtful comments, in addition to Josh Angrist, Alan
Barreca, Sandy Black, Colin Cameron, Trudy Ann Cameron, Scott Carrell,
Stacey Chen, Ben Hansen, Hilary Hoynes, Doug Miller, Marianne Page,
Chris Rohlfs, Peter Siminski, Ann Huff Stevens, Joe Stone, Matt Taylor,
Glen Waddell, and seminar and conference participants at UC-Davis,
University of Oregon, the 2010 WEAl Conference, the 2010 San Francisco
Fed Applied Micro Conference, and the 2011 SOLE meetingS. Special thanks
to Josh Angrist and Stacey Chen for providing us with results based on
their restricted-use U.S. Census data and to Chris Rohlfs for sharing
his NCRP code with us.
Lindo: Assistant Professor of Economics, University of Oregon,
University of Wollongong, NBER, and IZA. Phone 1-541-316-8343, Fax
1-541-346-1243, E-mail
[email protected]
Stoecker: Department of Economics, University of California, Davis,
One Shields Ave., Davis, CA 95616. Phone 530-400-7584, Fax 530-752-9382,
E-mail
[email protected]
(1.) For example, researchers have considered the effects of
punishments for infractions (Drago, Galbiati, and Vertrova 2009; Levitt
1998), policing (levitt 1997, 2002; MeCrary 2002; Yang 2008), punishment
(Hansen 2011; Lee and McCrary 2009) temporary income shocks (Foley 2011;
Miguel 2005), unemployment (Gould, Weinberg, and Mustard 2002; Mocan and
Bali 2010), inequality (Kelly 2000), drugs and alcohol (Carpenter 2007;
Carpenter and Dobkin 2008; Grogger and Willis 2000), neighborhoods
(Kling, Ludwig, and Katz 2004; Ludwig, Duncan, and Hirschfield 2001),
guns (Duggan 2001; Duggan, Hjalmarsson, and Jacob 2011), sporting events
and movies (Card and Dahl 2009; Dahl and DellaVigna 2009; Rees and
Schnepel 2009), casinos (Grinols and Mustard 2006), and incapacitation
(Dahl and DellaVigna 2009; Jacob and Lefgren 2003).
(2.) For example, using silhouettes in place of bulls-eye targets.
Slone and Friedman (2008) describe modern training as preparing soldiers
"to react within a split-second of any provocative activity and [to
shut down] emotions."
(3.) In a similar manner, this training may in part be responsible
for some of the violent conflicts among fellow servicemen. In Another
Brother, Greg Payton describes one such conflict:
We had been brought to Vietnam for violence, for violent
purposes, so it wasn't unusual for us to be violent
amongst ourselves you know. I remember the first
time I got shot at it was Christmas Eve and an African
American GI had a fight with a white GI. The white
GI went back to his hooch and he got his weapon. We
heard a weapon being loaded. Instinctively we hit the
ground and he opened up automatic fire. It was just
by split seconds that we weren't all killed.
(4.) Vietnam-era mobilization has also been shown to affect family
formation (BRier and Schmidt 2011), which may also contribute to impacts
on crime.
(5.) Rohlfs (2006) is the only prior work to use plausibly
exogenous variation to consider the effects of military service on
incarceration in the United States. In this study, in which he compares
the fraction of Vietnam Era draft eligible inmates in prison to the
fraction expected based on cohorts not subjected to the drafts, he finds
imprecise effects on overall rates of incarceration. Our study offers
several advantages over this work. First, we improve precision by using
within-cohort variation provided by the draft lotteries instead of a
cross-cohort difference-in-differences framework. This further enables
us to use non-affected cohorts as a robustness check to verify that our
results are not driven by the particular sets of birthdays selected in
the drafts. In addition, our outcome variable lends itself to a natural
interpretation, providing a direct estimate of the effect of draft
eligibility on the probability of incarceration in the survey years.
Finally, we present a more-comprehensive exploration of the effects
of draft eligibility on crime by separately considering its effects on
violent crime, drug-related crime, property-related crime, and
public-order crime.
(6.) Information on the details of the Vietnam Draft lottery can be
found at the Selective Service Website http://www.sss.gov/lotterl.htm
and in Flynn (1993) and Baskir and Strauss (1978).
(7.) While it is desirable to control for other covariates to
increase the precision of estimates, Angrist (1989) suggests that it is
not necessary to avoid bias since there is no correlation between draft
lottery status and characteristics besides subsequent veteran status.
(8.) That is, we regress whether an individual is a veteran on
whether an individual was draft eligible.
(9.) In particular, we assume [MATHEMATICAL EXPRESSION NOT
REPRODUCIBLE IN ASCII], which is likely to hold since the estimates are
based on independent samples, yielding [MATHEMATICAL EXPRESSION NOT
REPRODUCIBLE IN ASCII]. Bootstrapping produces nearly identical
standard-error estimates.
(10.) In contrast to these studies focusing on the United States,
Siminski (forthcoming) finds no evidence of similar effects for
Australia where there was no GI Bill.
(11.) Bedard and Deschenes (2006) provide a notable exception,
finding that military service in World War II and the Korean War led to
increased mortality due to increased smoking.
(12.) Because of confidentiality requirements, we do not have
direct access to these data. These results are based on specifications
that Josh Angrist and Stacey Cben have generously run for us. Angrist
and Chen (2011) also explore a specification in which the effects are
interacted with groups of lottery numbers. They find that these
additional instruments do not increase precision. For this reason, we
focus on the single instrument case which simplifies statistical
inference for the two-sample instrumental-variable estimates.
(13.) We follow the National Prisoner Statistics offense code
categorization. Violent crimes include any attempt at murder,
manslaughter, kidnapping, rape, robbery, assault, or extortion.
Drug-related crimes include traffic in or possession of drugs. Property
crimes include robbery, extortion. burglary, auto theft, fraud, larceny,
embezzlement, any stolen property crime, and drug trafficking. Finally,
public order crimes are more varied but primarily consist of weapons
violations and serious traffic offenses.
(14.) Broadly speaking, crime rates and incarceration rates rose
dramatically between 1979 and 1991. This is also true for the 1948-1952
cohorts that are the focus of this study. Given that the increase for
the 1948-1952 cohorts was a part of a broader social change that is not
well captured by the variables in our model (draft eligibility and
month-by-year-of-birth fixed effects), our explanatory power becomes
weaker and weaker over time, leading to larger and larger standard-error
estimates.
(15.) Correlational evidence based on the 1980 Census suggests a
small but significant negative effect of service in Vietnam on being
observed in a correctional facility.
(16.) We cannot use earlier cohorts in this falsification exercise
because earlier VSUS reports do not provide birth data by month, gender,
and race.
(17.) of particular concern, although the evidence is based on a
very small sample, Kuziemko (2008) presents suggestive evidence that men
with low lottery numbers may have engaged in delinquent behaviors to
avoid being drafted. She also examines Georgia prison admissions data
and finds that men with low lottery numbers in the non-binding 1972
lottery were over-represented. We also examine the 1972 lottery as a
robustness check and find no detectable relationship between low lottery
number and being incarcerated for the serious crimes that would have
kept an offender in prison until the 1979 inmate survey. One possible
reconciliation of our findings is that while some men may have
"dodged down" into prison to avoid conscription, they did not
commit the serious crimes with multi-year sentences we examine here.
(18.) As another robustness check, we have considered the
interaction between incarceration for a violent crime and non-Army
military service as an outcome. Since nearly all drafted men served in
the Army, we should not find significant effects on this outcome.
Indeed, we find draft eligibility significantly raises the probability
of being a violent offender and an Army veteran and has no effect on
being a violent offender and a veteran from another branch of service.
(19.) There are two potential explanations for why there could be
effects on arrests soon after the war but not later on. It may be the
case that the effects of military service on criminal behavior fade out
as veterans spend more time as civilians. Or this finding may simply
reflect an incapacitation effect--we may be less likely to observe
impacts on prison admissions in the 1980s because men who were affected
most were already incarcerated in earlier years, as evidenced by the
significant impacts we found on the prison population in 1979.
(20.) Instead extrapolating to the 2.5 million white veterans from
the 1948-1952 cohorts, our estimates suggest that military service
contributed to an additional 8,500 men being incarcerated for a violent
crime in 1979. As an alternative exercise, one could extrapolate from
our results to the smaller subset of males who were induced to serve by
the draft. Given that the draft caused many males to volunteer, however,
the effect of the draft on military service is unknown (despite the fact
that the effect of eligibility is easily estimated). Counts of veterans
are authors' calculations based on the 2000 Census.
(21.) At the same time, we cannot rule out the possibility the
military service is beneficial to some individuals and detrimental to
others in a way that leads to these opposite-signed effects.
(22.) For more details, see http://www.army.mil/news/2010/06/17/
40960-iraqi-role-players-add-realism-to-cadet-training/
(23.) These statistics are congressional testimony by Thomas R.
Insel before the Committee on Oversight and Government Reform in 2007.
Available online at: http://
www.hhs.gov/aslltestify120071051t20070524a.html
(24.) In response to a survey from the Warrior Transition Unit at
Fort Hood, where physically and mentally wounded soldiers are sent to
heal, 41% of commanding officers thought more than half of soldiers
claiming to have symptoms of posttraumatic stress disorder were faking
or exaggerating versus 11% of nurse case managers.
(25.) Details on these courts can be found at the Veterans
Treatment Court Clearinghouse which is hosted by the National
Association of Drug Court Professionals.
TABLE 1
Estimated First-Stage Effects of Draft Eligibility on Military Service
Cohort 1944 1945 1946 1947
(1) (2) (3) (4)
Panel A: Whites
Draft-eligibility -0.0047 * 0.0021 0.0145 *** 0.0344 ***
effect (0.0027) (0.0028) (0.0026) (0.0026)
Observations 174,222 172,160 207,805 234,219
F-statistic 3 1 31 179
Panel B: Nonwhites
Draft-eligibility 0.0031 -0.0028 0.0056 0.0212 ***
effect (0.0076) (0.0075) (0.0077) (0.0072)
Observations 20,500 21,405 23,454 27,008
F-statistic 0 0 1 9
Cohort 1948 1949 1950 1951
(5) (6) (7) (8)
Panel A: Whites
Draft-eligibility 0.0577 *** 0.0743 *** 0.1332 *** 0.1384 ***
effect (0.0023) (0.0027) (0.0028) (0.0028)
Observations 220,891 224,130 223,984 232,348
F-statistic 616 753 2213 2522
Panel B: Nonwhites
Draft-eligibility 0.0327 *** 0.0492 *** 0.0893 *** 0.0959 ***
effect (0.0067) (0.0067) (0.0059) (0.0060)
Observations 28,272 30,321 31,942 31,162
F-statistic 24 54 230 256
Cohort 1952 1948-1952
(9) (10)
Panel A: Whites
Draft-eligibility 0.1685 *** 0.1134 ***
effect (0.0030) (0.0018)
Observations 240,198 1,141,551
F-statistic 3146 3869
Panel B: Nonwhites
Draft-eligibility 0.0964 *** 0.0734 ***
effect (0.0064) (0.0028)
Observations 33,113 154,810
F-statistic 228 707
Notes: Results are based on restricted-use U.S. Census data from 2000.
Estimates show the impact of draft eligibility on military service by
birth cohort and race. Specifications are at the individual level,
include month-by-year-of-birth fixed effects, cluster standard-error
estimates on lottery numbers. and are weighted using Census sampling
weights.
* Significant at 10%; ** significant at 5%; *** significant at 1%.
TABLE 2
Estimated Incarceration Probabilities, Males Born 1948-1952
Race White
Draft Eligibility Eligible Ineligible Difference
Panel A: Aggregated Survey Waves
All crime 0.0060 0.0060 0.0000
(0.0003)
Violent crime 0.0024 0.0021 0.0003 **
(0.0001)
All nonviolent crime 0.0036 0.0039 -0.0003
(0.0002)
Drug crime 0.002 0.0021 -0.0001
(0.0002)
Property crime 0.0033 0.0032 0.0001
(0.0002)
Public order crime 0.0008 0.0008 0.0000
(0.0001)
Panel B: 1979 Survey
All crime 0.0032 0.0033 -0.0001
(0.0002)
Violent crime 0.0015 0.0012 0.0003 *
(0.0001)
All nonviolent crime 0.0017 0.0020 -0.0004 **
(0.0002)
Drug crime 0.0003 0.0003 0.0000
(0.0001)
Property crime 0.0014 0.0013 0.0001
(0.0001)
Public order crime 0.0002 0.0002 0.0001
(0.0001)
Panel C: 1986 Survey
All crime 0.0036 0.0038 -0.0002
(0.0003)
Violent crime 0.0023 0.002 0.0003
(0.0002)
All nonviolent crime 0.0014 0.0019 -0.0005 **
(0.0002)
Drug crime 0.0004 0.0006 -0.0002 **
(0.0001)
Property crime 0.0020 0.0021 -0.0001
(0.0002)
Public order crime 0.0006 0.0006 0.0000
(0.0001)
Panel D: 1991 Survey
All crime 0.0112 0.0109 0.0003
(0.0007)
Violent crime 0.0034 0.0031 0.0004
(0.0003)
All nonviolent crime 0.0078 0.0079 -0.0001
(0.0006)
Drug crime 0.0054 0.0055 -0.0001
(0.0005)
Property crime 0.0066 0.0063 0.0003
(0.0005)
Public order crime 0.0015 0.0016 -0.0001
(0.0003)
Race Nonwhite
Draft Eligibility Eligible Ineligible Difference
Panel A: Aggregated Survey Waves
All crime 0.0337 0.0323 0.0014
(0.0014)
Violent crime 0.0174 0.0161 0.0013
(0.001)
All nonviolent crime 0.0163 0.0162 0.0002
(0.001)
Drug crime 0.0064 0.0064 0.0000
(0.0008)
Property crime 0.0200 0.0192 0.0009
(0.0011)
Public order crime 0.0043 0.0035 0.0008
(0.0005)
Panel B: 1979 Survey
All crime 0.0254 0.0257 -0.0004
(0.0015)
Violent crime 0.0123 0.013 -0.0007
(0.0011)
All nonviolent crime 0.0131 0.0128 0.0003
(0.0011)
Drug crime 0.0018 0.0014 0.0005
(0.0004)
Property crime 0.0129 0.0133 -0.0004
(0.0011)
Public order crime 0.0016 0.0013 0.0003
(0.0004)
Panel C: 1986 Survey
All crime 0.0256 0.0282 -0.0025
(0.0019)
Violent crime 0.0161 0.0175 -0.0015
(0.0015)
All nonviolent crime 0.0096 0.0106 -0.0011
(0.0012)
Drug crime 0.0021 0.0024 -0.0003
(0.0006)
Property crime 0.0158 0.0175 -0.0017
(0.0015)
Public order crime 0.0030 0.0030 0.0001
(0.0007)
Panel D: 1991 Survey
All crime 0.0501 0.0429 0.0072 **
(0.0035)
Violent crime 0.0238 0.0178 0.006
(0.0023)
All nonviolent crime 0.0263 0.0251 0.0012
(0.0026)
Drug crime 0.0152 0.0154 -0.0002
(0.0021)
Property crime 0.0314 0.0267 0.0048 *
(0.0027)
Public order crime 0.0083 0.0063 0.0020
(0.0014)
Notes: Observations are at the exact day of birth by survey year
level. Incarceration data are from the 1979, 1986, and 1991 SISFCF
and birth data are from the VSUS. Estimated standard errors,
clustered on lottery number, are shown in parentheses.
* Significant at 10%; ** significant at 5%; *** significant at 1%.
TABLE 3
Estimated Effects of Draft Eligibility and Military Service on the
Probability of Incarceration, White Males Born 1948-1952
Survey Years All 1979
(1) (2)
Panel A: Incarceration for a Violent Crime
Estimated effect of eligibility 0.00030 * 0.00038 **
(0.00016) (0.00016)
TSIV estimated effect of service 0.00269 * 0.00340 **
(0.00142) (0.00144)
Observations 5,481 1,827
Panel B: Incarceration for a Nonviolent Crime
Estimated effect of eligibility -0.00026 -0.00033 *
(0.00024) (0.00018)
TSIV estimated effect of service -0.00228 -0.00299 *
(0.00211) (0.00164)
Observations 5,481 1,827
Panel C.: Incarceration for Any Crime
Estimated effect of eligibility 0.00005 0.00005
(0.00028) (0.00025)
TSIV estimated effect of service 0.00041 0.00041
(0.00252) (0.00226)
Observations 5,481 1,827
Survey Years 1986 1991
(3) (4)
Panel A: Incarceration for a Violent Crime
Estimated effect of eligibility 0.00016 0.00036
(0.00023) (0.00036)
TSIV estimated effect of service 0.00145 0.00323
(0.00204) (0.00322)
Observations 1,827 1,827
Panel B: Incarceration for a Nonviolent Crime
Estimated effect of eligibility -0.00053 *** 0.00009
(0.00019) (0.00064)
TSIV estimated effect of service -0.00469 *** 0.00084
(0.00172) (0.00568)
Observations 1,827 1,827
Panel C.: Incarceration for Any Crime
Estimated effect of eligibility -0.00036 0.00046
(0.00030) (0.00072)
TSIV estimated effect of service -0.00324 0.00407
(0.00264) (0.00641)
Observations 1,827 1,827
Notes: Reduced-form estimates use observations at the exact day of
birth by survey year level. Incarceration data are from the 1979,
1986, and 1991 SISFCF and birth data are from the VSUS. All
specifications include month-by-year-of-birth fixed effects and
survey-year fixed effects and weight by the number of individuals
represented by the cell. All drafted cohorts include birth years
ranging from 1944 to 1952. Estimated standard errors. clustered on
lottery number, are shown in parentheses. The two-sample
instrumental-variable estimates of the effect of military service on
incarceration use the first-stage estimates shown in Table 1.
* Significant at 10%; ** significant at 5%; *** significant at 1%.
TABLE 4
Estimated Effects of Draft Eligibility and Military Service on the
Probability of Incarceration, Nonwhite Males Born 1948-1952
Survey Years All 1979
(1) (2)
Panel A: Incarceration for a Violent Crime
Estimated effect of eligibility 0.00183 * -0.00058
(0.00097) (0.00114)
TSIV estimated effect of service 0.02537 * -0.00799
(0.01354) (0.01582)
Observations 5,481 1,827
Panel B: Incarceration for a Nonviolent Crime
Estimated effect of eligibility 0.00024 0.00047
(0.00115) (0.00118)
TSIV estimated effect of service 0.00335 0.00647
(0.01601) (0.01638)
Observations 5,481 1,827
Panel C: Incarceration for Am, Crime
Estimated effect of eligibility 0.00207 -0.00011
(0.00156) (0.00172)
TSIV estimated effect of service 0.02872 -0.00152
(0.02161) (0.02387)
Observations 5,481 1,827
Survey Years 1986 1991
(3) (4)
Panel A: Incarceration for a Violent Crime
Estimated effect of eligibility -0.00093 0.00698
(0.00150) (0.00247)
TSIV estimated effect of service -0.01288 0.09697
(0.02085) (0.03434)
Observations 1,827 1,827
Panel B: Incarceration for a Nonviolent Crime
Estimated effect of eligibility -0.00029 0.00055
(0.00134) (0.00293)
TSIV estimated effect of service -0.00400 0.00759
(0.01867) (0.04068)
Observations 1,827 1,827
Panel C: Incarceration for Am, Crime
Estimated effect of eligibility -0.00121 0.00753 *
(0.00191) (0.00388)
TSIV estimated effect of service -0.01687 0.10456 *
(0.02657) (0.05389)
Observations 1,827 1,827
Notes: See Table 3.
* Significant at 10%; ** significant at 5%; *** significant at 1%.
TABLE 5
Estimated Effects of Draft Eligibility on the Probability of
Incarceration (per 10,000), White Males Born 1948-1952, Narrow Crime
Definitions
Survey Years All 1979 1986 1991
(1) (2) (3) (4)
Panel A: Violent Crimes
Sex crime 0.03374 -0.13205 0.03552 0.19774
(0.31716) (0.22670) (0.51963) (0.76831)
Murder 0.40634 0.17080 0.41639 0.63181
(0.34170 (0.34953) (0.50867) (0.84605)
Manslaughter 0.13382 0.21524 -0.10981 0.29604
(0.13928) (0.19748) (0.28355) (0.24733)
Kidnapping 0.45351 ** 0.48381 ** 0.56226 * 0.31447
(0.19080) (0.21809) (0.29373) (0.38196)
Extortion 0.01105 -0.04555 0.07837 0.00034
(0.06992) (0.03297) (0.05609) (0.20128)
Robbery 0.85441 * 0.81421 * 0.63964 1.10938
(0.45519) (0.43910) (0.56057) (1.09291)
Assault 0.10965 0.67652 ** -0.23495 -0.11162
(0.26486) (0.31373) ((1.42690) (0.61535)
Panel B: Property Crimes
Burglary -0.07211 0.08748 -0.97245 * 0.66864
(0.31622) (0.40238) (0.57465) (0.67238)
Auto theft 0.04796 0.10163 -0.10132 0.14358
(0.12995) (0.13440) (0.14794) (0.33755)
Arson 0.06069 0.06986 -0.05977 0.17199
(0.15979) (0.10230) (0.20011) (0.41651)
Fraud 0.07990 0.13674 0.06775 0.03521
(0.19691) (0.23200 (0.26385) (0.45214)
Larcency -0.11887 0.17309 -0.61080 * 0.08111
(0.19405) (0.21484) (0.34528) (0.47256)
Stolen property 0.00665 0.26884 * -0.43651 0.18762
offense
(0.13211) (0.16185) (0.26825) (0.23332)
Property damage -0.06099 0.01960 -0.21908 0.01649
(0.05184) (0.04740) (0.13522) (0.06973)
Illegal entry -0.08197 ** -0.00436 -0.11659 * -0.12495
(0.04055) (0.04258) (0.06728) (0.09374)
Panel C: Drug Crimes
Drug trafficking 0.39876 0.07963 -0.34441 1.46104
(0.75063) (0.25094) (0.36512) (2.18537)
Drug possession -0.03203 0.03931 -0.51008 * 0.37467
(0.43720) (0.20912) (0.29064) (1.27514)
Notes: See Table 3.
* Significant at 10%: ** significant at 5%: *** significant at 1%.
TABLE 6
Estimated Effects of Draft Eligibility on the Probability of
Incarceration (per 10,000), Nonwhite Males Born 1948-1952, Narrow
Crime Definitions
Survey Years All 1979 1986 1991
(1) (2) (3) (4)
Panel A. Violent Crimes
Sex crime 0.17018 0.38616 -0.51407 0.63844
(0.26033) (0.31434) (0.44293) (0.57886)
Murder 0.17532 -0.12156 -0.20916 0.85668
(0.31573) (0.39409) (0.55667) (0.75920)
Manslaughter 0.06989 -0.07122 -0.01048 0.29136
(0.15359) (0.12900) (0.27544) (0.35614)
Kidnapping 0.17064 0.07405 -0.04711 0.48497
(0.18084) (0.15431) (0.21741) (0.48335)
Extortion -0.00447 0.06481 -0.08023 0.00200
(0.05761) (0.04665) (0.05642) (0.15825)
Robbery 0.78956 -0.66841 -0.60538 3.64246
(0.52098) (0.57406) (0.70337) (1.33056)
Assault -0.02074 -0.07_555 0.49501 -0.48168
(0.26517) (0.30925) (0.46501) (0.57096)
Panel B: Property Crimes
Burglary 0.84968 ** 0.87866 * 1.04852 * 0.62186
(0.33497) (0.46072) (0.61290) (0.61581)
Auto theft 0.06487 0.07476 0.06209 0.05776
(0.13398) (0.11717) (0.11602) (0.37490)
Arson 0.00660 -0.02283 0.11411 -0.07148
(0.13530) (0.07513) (0.12706) (0.38480)
Fraud -0.18897 -0.19071 -0.77946 *** 0.40326
(0.19793) (0.18708) (0.28498) (0.49588)
Larcency -0.18514 0.04169 -0.23127 -0.36585
(0.23576) (0.28554) (0.45778) (0.48803)
Stolen property 0.25446 * 0.10392 0.02929 0.63017 *
offense (0.14225) (0.14835) (0.22070) (0.34554)
Property damage -0.02929 -0.02694 0.02904 -0.08998
(0.05190) (0.03873) (0.07813) (0.13224)
Illegal entry 0.03374 0.07862 -0.04960 0.07222
(0.07518) (0.09159) (0.20067) (0.07176)
Panel C. Drug Crimes
Drug trafficking 0.04325 0.07496 0.20255 -0.14777
(0.45920) (0.25159) (0.33590) (1.37148)
Drug possession 0.12018 0.19166 -0.14244 0.31132
(0.28846) (0.17275) (0.24559) (0.81631)
Notes: See Table 3.
* Significant at 10%: ** significant at 5%: *** significant at 1%.
TABLE 7
Robustness Check Applying Lotteries to Unaffected Cohorts: Estimated
Effects of Draft Eligibility Placebo on the Probability of
Incarceration
Cohort's Lottery 1944-1950
Applied Cohorts Used 1942, 1943, 1951-1959
In Analysis
All 1979 1986 1991
Survey Years (1) (2) (3) (4)
Panel A: Incarceration for a Violent Crime, White Males
Estimated effect of -0.00012 -0.00004 -0.00001 -0.00031
eligibility (0.00011) (0.00011) (0.00015) (0.00025)
Observations 12,051 4,017 4,017 4.017
Panel B: Incarceration for n Nonviolent Crime, White Males
Estimated effect of -0.00005 -0.00009 -0.00005 -0.00001
eligibility (0.00015) (0.00013) (0.00016) (0.00042)
Observations 12,051 4,017 4,017 4,017
Panel C: Incarceration for a Violent Crime, Nonwhite Males
Estimated effect of -0.00045 0.00048 0.00104 -0.00288 *
eligibility (0.00066) (0.00069) (0.00114) (0.00155)
Observations 12,051 4,017 4,017 4,017
Panel D: Incarceration for a Nonviolent Crime, Nonwhite Males
Estimated effect of -0.00011 -0.00037 0.00052 -0.00049
eligibility (0.00074) (0.00070) (0.00087) (0.00190)
Observations 12,051 4,017 4,017 4,017
Cohort's Lottery 1951
Applied Cohorts Used 1942-1950, 1952-1959
In Analysis
All 1979 1986 1991
Survey Years (5) (6) (7) (8)
Panel A: Incarceration for a Violent Crime, White Males
Estimated effect of 0.00000 -0.00001 -0.00012 0.00014
eligibility (0.00008) (0.00008) (0.00013) (0.00021)
Observations 18,615 6,205 6,205 6,205
Panel B: Incarceration for n Nonviolent Crime, White
Estimated effect of -0.00001 -0.00001 0.00019 -0.00022
eligibility (0.00012) (0.00010) (0.00012) (0.00034)
Observations 18,615 6,205 6,205 6,205
Panel C: Incarceration for a Violent Crime, Nonwhite Males
Estimated effect of 0.00047 0.00061 0.00013 0.00066
eligibility (0.00059) (0.00067) (0.00092) (0.00130)
Observations 18,615 6,205 6,205 6,205
Panel D: Incarceration for a Nonviolent Crime, Nonwhite Males
Estimated effect of -0.00100 -0.00028 0.00006 -0.00278 *
eligibility (0.00061) (0.00061) (0.00069) (0.00156)
Observations 18,615 6,205 6,205 6,205
Cohort's Lottery 1952
Applied Cohorts Used 1942-1951, 1953-1959
In Analysis
All 1979 1986 1991
Survey Years (9) (10) (11) (12)
Panel A: Incarceration for a Violent Crime, White Males
Estimated effect of 0.00008 0.00000 0.00020 0.00004
eligibility (0.00010) (0.00009) (0.00015) (0.00024)
Observations 18,624 6,208 6,208 6,208
Panel B: Incarceration for n Nonviolent Crime, White
Estimated effect of -0.00004 -0.00009 0.00005 -0.00009
eligibility (0.00014) (0.00011) (0.00014) (0.00038)
Observations 18,624 6,208 6,208 6,208
Panel C: Incarceration for a Violent Crime, Nonwhite Males
Estimated effect of -0.00051 -0.00014 0.00019 -0.00157
eligibility (0.00060) (0.00061) (0.00097) (0.00131)
Observations 18,624 6,208 6,208 6,208
Panel D: Incarceration for a Nonviolent Crime, Nonwhite Males
Estimated effect of 0.00050 -0.00033 0.00027 0.00155
eligibility (0.00070) (0.00064) (0.00074) (0.00185)
Observations 18,624 6,208 6,208 6,208
Notes: See Table 3.
* Significant at 10%; ** significant at 5%: *** significant at 1%.
TABLE 8
Robustness Check Using Nonbinding Lotteries for 1953-1956 Birth
Cohorts: Estimated Effects of Draft Eligibility on the Probability of
Incarceration
Highest APN Applied 95
Survey Years All 1979 1986 1991
(1) (2) (3) (4)
Panel A: Incarceration for a Violent Crime, White Males
Estimated effect of -0.00002 0.00014 0.00005 -0.00025
eligibility (0.00020) (0.00018) (0.00031) (0.00043)
Observations 4,383 1,461 1,461 1,461
Panel B: Incarceration: for a Nonviolent Crime, White Males
Estimated effect of 0.00033 -0.00022 0.00043 0.00079
eligibility (0.00031) (0.00023) (0.00031) (0.00080)
Observations 4,383 1,461 1,461 1,461
Panel C: Incarceration for a Violent Crime, Nonwhite Males
Estimated effect of 0.00142 -0.00088 0.00130 0.00386
eligibility (0.00132) (0.00145) (0.00197) (0.00306)
Observations 4,383 1,461 1,461 1,461
Panel D: Incarceration for a Nonviolent Crime, Nonwhite Males
Estimated effect of 0.00067 0.00214 -0.00103 0.00090
eligibility (0.00129) (0.00154) (0.00149) (0.00328)
Observations 4,383 1,461 1,461 1,461
Highest APN Applied 125
Survey Years All 1979 1986 1991
(5) (6) (7) (8)
Panel A: Incarceration for a Violent Crime, White Males
Estimated effect of -0.00022 0.00000 0.00002 -0.00068 *
eligibility (0.00018) (0.00017) (0.00028) (0.00040)
Observations 4,383 1,461 1,461 1,461
Panel B: Incarceration: for a Nonviolent Crime, White Males
Estimated effect of 0.00041 -0.00019 0.00042 0.00100
eligibility (0.00027) (0.00021) (0.00027) (0.00071)
Observations 4,383 1,461 1,461 1,461
Panel C: Incarceration for a Violent Crime, Nonwhite Males
Estimated effect of 0.00094 -0.00040 0.00164 0.00157
eligibility (0.00119) (0.00139) (0.00179) (0.00272)
Observations 4,383 1,461 1,461 1,461
Panel D: Incarceration for a Nonviolent Crime, Nonwhite Males
Estimated effect of 0.00105 0.00134 -0.00099 0.00280
eligibility (0.00122) (0.00134) (0.00139) (0.00328)
Observations 4,383 1,461 1,461 1,461
Highest APN Applied 195
Survey Years All 1979 1986 1991
(9) (10) (11) (12)
Panel A: Incarceration for a Violent Crime, White Males
Estimated effect of 0.00008 0.00008 0.00017 0.00001
eligibility (0.00017) (0.00016) (0.00025) (0.00040)
Observations 4,383 1,461 1,461 1,461
Panel B: Incarceration: for a Nonviolent Crime, White Males
Estimated effect of 0.00049 ** 0.00009 0.00028 0.00109 *
eligibility (0.00025) (0.00020) (0.00024) (0.00066)
Observations 4,383 1,461 1,461 1,461
Panel C: Incarceration for a Violent Crime, Nonwhite Males
Estimated effect of -0.00075 -0.00087 0.00140 -0.00276
eligibility (0.00107) (0.00129) (0.00172) (0.00244)
Observations 4,383 1,461 1,461 1,461
Panel D: Incarceration for a Nonviolent Crime, Nonwhite Males
Estimated effect of 0.00000 0.00168 0.00082 -0.00249
eligibility (0.00116) (0.00118) (0.00138) (0.00296)
Observations 4,383 1,461 1,461 1,461
Notes: See Table 3.
* Significant at 10%; ** significant at 5%n; *** significant at 1%.
TABLE 9
Analysis Using NCRP Prison Admissions Data: Estimated Effects of
Draft Eligibility and Military Service on Incarceration
Years 1983-1991 1983 1984 1985
(1) (2) (3) (4)
Panel A: Incarceration for a Violent Crime, White Males
Estimated effect of -0.014 0.150 -0.034 0.144
eligibility per 10,000 (0.043) (0.134) (0.138) (0.140)
Observations 16,443 1,827 1,827 1,827
Panel B: Incarceration for a Nonviolent Crime, White Males
Estimated effect of -0.020 0.003 0.266 0.237
eligibility per 10,000 (0.088) (0.191) (0.176) (0.193)
Observations 16,443 1,827 1,827 1,827
Panel C. Incarceration for a Violent Crime, Nonwhite Males
Estimated effect of -0.335 -0.258 -0.520 -0.259
eligibility per 10,000 (0.330) (0.779) (0.851) (0.975)
Observations 16,443 1,827 1,827 1,827
Panel D: Incarceration for a Nonviolent Crime, Nonwhite Males
Estimated effect of 0.198 -1.459 1.161 0.523
eligibility per 10,000 (0.611) (1.122) (1.222) (1.382)
Observations 16,443 1,827 1,827 1,827
Years 1986 1987 1988
(5) (6) (7)
Panel A: Incarceration for a Violent Crime, White Males
Estimated effect of -0.142 -0.017 -0.092
eligibility per 10,000 (0.140) (0.129) (0.147)
Observations 1,827 1,827 1,827
Panel B: Incarceration for a Nonviolent Crime, White Males
Estimated effect of 0.158 -0.390 * -0.304
eligibility per 10,000 (0.236) (0.235) (0.252)
Observations 1,827 1,827 1,827
Panel C. Incarceration for a Violent Crime, Nonwhite Males
Estimated effect of -1.287 -1.269 0.618
eligibility per 10,000 (0.934) (0.893) (1.034)
Observations 1,827 1,827 1,827
Panel D: Incarceration for a Nonviolent Crime, Nonwhite Males
Estimated effect of 0.315 -1.468 -0.195
eligibility per 10,000 (1.446) (1.461) (1.818)
Observations 1,827 1,827 1,827
Years 1989 1990 1991
(8) (9) (10)
Panel A: Incarceration for a Violent Crime, White Males
Estimated effect of -0.304 ** 0.024 0.144
eligibility per 10,000 (0.147) (0.138) (0.134)
Observations 1,827 1,827 1,827
Panel B: Incarceration for a Nonviolent Crime, White Males
Estimated effect of -0.067 0.010 -0.092
eligibility per 10,000 (0.232) (0.272) (0.240)
Observations 1,827 1,827 1,827
Panel C. Incarceration for a Violent Crime, Nonwhite Males
Estimated effect of -0.708 -0.611 1.277
eligibility per 10,000 (0.835) (0.879) (0.862)
Observations 1,827 1,827 1,827
Panel D: Incarceration for a Nonviolent Crime, Nonwhite Males
Estimated effect of -0.138 2.181 0.867
eligibility per 10,000 (1.613) (1.791) (1.595)
Observations 1,827 1,827 1,827
Notes: NCRP prison admissions data are restricted to individuals who
are admitted due to a court commitment. The analysis is conducted in
the manner described in Table 3.
* Significant at 10%; ** significant at 5%; *** significant at 1%.
