Paternity deferments and the timing of births: U.S. natality during the Vietnam war.
Kutinova, Andrea
I. BACKGROUND
During the conflict in Vietnam, men between 18.5 and 25 yr of age
were subject to the draft. Several exemptions to this rule existed. For
example, students were exempt. Importantly for the purposes of this
study, married men with dependents could also obtain a deferment from
the draft, and the particulars of this policy underwent substantial
changes in the 1960s. In August 1965, President Johnson issued Executive
Order 11241, which formally eliminated deferments for childless men who
got married after August 26, 1965, and in October 1965, the Selective
Service declared that childless married men (irrespective of the date of
marriage) were to be called up. Both announcements came as a surprise
(New York Times 1965a). Since married men with children remained exempt,
the declarations provided a strong incentive for young couples to
conceive a (first-born) child. Before August 1965, marriage had been a
sufficient condition for a deferment. Even just a few hours before the
August 26 midnight deadline, desperate couples tried to make use of this
provision by quickly scheduling their wedding. Between August and
October, couples who had missed the deadline had to satisfy an
additional condition--conceiving a child. Childless men who got married
in this period were still subject to the draft and so had an incentive
to conceive a child. In October 1965, the risk of induction was further
extended to all couples who had remained childless. Finally, in April
1970, the family deferments were entirely eliminated by Executive Order
11527 (The Selective Service System, Office of Public and
Intergovernmental Affairs 2004).
Past research has demonstrated that taxes and expenditure programs
can affect fertility (e.g., Whittington, Alm, and Peters 1990; see also
Milligan 2005, for an excellent review) as well as the timing of
delivery (Dickert-Conlin and Chandra 1999). The goal of this article was
to provide additional evidence on the responsiveness of childbearing to
incentives embedded in public policy by studying a dramatic, yet
unexamined government intervention--the effects of the Vietnam War paternity deferments on the decision to conceive a first-born child. As
discussed in the popular press, Vice President Dick Cheney's first
daughter, Elizabeth, was born 9 mo 2 d after the Selective Service
System announced that childless married men were to be drafted (Boston
Globe 2000; Slate Chatterbox 2004). Did draft-eligible men strategically
react to the announcement? And, if so, how widespread and fast was the
response?
To my knowledge, no one has investigated the impacts of the Vietnam
draft on natality. Using the Vietnam draft rules to identify a causal
effect, however, I build on several prior studies. Angrist, for example,
uses the exogeneity of the Vietnam draft rules to identify the effects
of military service on lifetime earnings (Angrist 1990; Angrist and Chen
2007) and to measure the racial differences in the value of military
service (Angrist 1991). Gullason (1989) and Card and Lemieux (2001,
2002) estimate the effects of the Vietnam draft on schooling, explicitly
recognizing that college attendance often served as a vehicle to avoid
the draft. Both studies find a significant effect of the probability of
being drafted on school enrollment.
The fact that the changes in the Selective Service rules were both
unexpected and widely publicized makes this an ideal example to study
the effects of policy on fertility decisions. Milligan (2005) argues
that the assumptions made about the timing of the response to policy are
arbitrary since a reaction will be delayed not only by a 9-mo
gestational lag but also by the time necessary for the diffusion of
information about the change in policy. In the case examined here,
however, the criticism seems less relevant. Newspaper clippings from
August 27, 1965, suggest that the issuance of the Executive Order 11241
did receive broad attention. For example, the story was listed on the
front pages of New York Times (1965c) and Washington Post (1965b). The
benefits of becoming a father were made explicit: "From now on, a
draft-age man who gets married and becomes a father before being called
into service will go into the same deferred class as other fathers"
(Washington Post 1965b, A12). Similarly, on October 27, 1965, one day
after the Selective Service declared that childless married men were to
be called up, the top U.S. newspapers commented on the policy change
(New York Times 1965a; Washington Post 1965a). (1) It is reasonable to
assume that the general public was well aware of the news.
Also, given the urgency of the situation for the potential
draftees, any behavioral response was likely to be fast. In the
mid-1960s, the risk of induction facing young American men was
increasing dramatically. In the year 1965, when the new policies were
announced, the number of men inducted each month increased by more than
sixfold from less than 6,000 to nearly 39,000 (Figure 1). And, as
anecdotal evidence suggests, young couples were ready to react almost
immediately. For example, after President Johnson's Executive Order
was issued on August 26, 1965, limiting the eligibility for marital
deferments to men married on or before that date, many couples quickly
scheduled their wedding in order to beat the midnight deadline (New York
Times 1965b).
Finally, information about the fecundity of the U.S. population in
the early 1960s confirms that young women were, on average, able to
conceive a child quickly. In the year 1960, 52% of Americans aged 20-24
yr were able to conceive within a month from trying, and 77% were
successful within 2 mo (Crist 2004). Thus, a fast and relatively strong
reaction to the Executive Order issuance and the Selective Service
announcement is realistic.
II. DATA AND METHODS
To empirically investigate the effects of the Vietnam draft on
natality, I focus on the impacts of President Johnson's Executive
Order 11241 and the October 1965 Selective Service announcement and make
use of the fact that these policies affected different groups of young
men differently. In particular, I use a difference-in-differences type
of approach and compare the effects of the policy changes on the
behavior of treatment and control groups of young men.
Ideally, all American men in the draft-eligible age would
constitute the treatment group. Unfortunately, however, the data set
most suitable for the study--the Vital Statistics of the United States (U.S. Department of Health, Education, and Welfare 1963-1977)--does not
provide detailed information on paternal characteristics. (2) Therefore,
I use maternal age as a proxy for the father's age and adjust for
the possibility of bias due to misclassification of some women into the
treatment and/or the control group. A new adjustment method developed in
Lewbel (2003) is ideal for the purpose at hand and is described in more
detail in the Correction for Misclassification section and the Technical
Appendix. It is worth foreshadowing here that the unadjusted results are
conservative since any misclassification into the treatment and/ or the
control group will bias the estimated treatment effect downward.
[FIGURE 1 OMITTED]
The Vital Statistics report the number of births for the following
age cohorts: younger than 15 yr, 15-19 yr, 20-24 yr, 25-29 yr, 30-34 yr,
35-39 yr, 40-44 yr, 4549 yr, and 50 yr and older. In my baseline model,
I use women aged 20-24 yr as the treatment group since only men up to 25
yr of age were eligible for the draft and since women, on average, tend
to be younger than their partners (Table 1). I exclude teenagers from
the baseline analysis since women younger than 15 yr were unlikely to be
affected by the government policy and since mothers aged 15-19 yr seem
diverse with respect to their fertility responsiveness (the attitudes
toward family planning will likely differ among women in this group).
Also, my calculations suggest that between 17.3% (year 1963) and 26.7%
(year 1968) of mothers aged 15-19 yr were single in the period under
study. The corresponding estimates are 5.7% and 8.3% for mothers aged
20-24 yr. (3) In an alternative specification, I add teenagers (15-19 yr
old) to the treatment group. Women aged 25-29 yr--with husbands likely
to be 26 yr or older and thus ineligible for the Vietnam draft--comprise
the control group.
To assess the validity of my treatment and control groups, I use
the U.S. Natality Detail Files for the years 1969-1971 (4) and calculate
the percentages of fathers aged 19-25 yr (the draft-eligible cohort) by
maternal age (Table 2). Maternal age is a reasonably good proxy for
paternal age. In particular, 65% of mothers aged 20-24 yr (the baseline
treatment group) had babies with fathers aged 19-25 yr in each of the
years 1969, 1970, and 1971. The corresponding percentage was 68% for
women aged 15-24 yr (an alternative treatment group) and 11% for mothers
in the 25- to 29-yr-old cohort (the control group). As I discuss
shortly, these misclassification probabilities derived from an
alternative data set prove useful in adjusting the baseline
difference-indifferences estimates.
Since the existence of children rather than their number played a
role in determining draft eligibility, I focus on the birth of a
first-born child when estimating the effects of the Executive Order and
the Selective Service announcement. Also, the outcome measure needs to
be corrected for the overall effects of the war on fertility. In
particular, it needs to isolate the potential changes in the number of
first births in reaction to the new deferment rules from the overall
changes in natality in a country where many young men had been sent to
war. (5) Therefore, I use the age-specific ratio of the number of
firstborn infants to all infants (reported by month and year of
delivery) as the dependent variable. If the 1965 declarations had a
significant effect on the fertility behavior of the potential draftees,
the "first-born infants-to-all infants" ratio should increase
in the summer of 1966 (about 9 mo after the policy changes were enacted)
for women in the treatment group and stay unchanged (or to increase
less) for women in the control group. Thus, a comparison of the monthly
first-born infants/all infants series (purged of a linear time trend and
seasonal variation) for the treatment and control groups yields an
estimate of the causal relationship between the new government draft
policies and fertility. In some of my robustness checks in the
following, I verify that the number of subsequent births is not driving
my results. In particular, I directly show that there is no effect of
the paternity deferments on the number of subsequent births and also
decompose the first-born infants-to-all infants ratio in order to allow
for a more flexible functional form. All these specification checks
support the robustness of the baseline results.
More formally, the baseline model is set up as follows:
[Y.sub.tj] = [alpha] + [beta] x [T.sub.j] + [gamma] x [M.sub.t] +
[delta]
x [T.sub.j] x [M.sub.t] + [[epsilon].sub.tj],
where t indexes time periods (months from January 1963 to December
1968) and j indexes cohorts (treatment or control). Y is the detrended
and deseasonalized first-born infants-to-all infants ratio; T is a dummy
variable denoting the treatment group membership (ages 20 24 yr in the
baseline specification); and M is a vector of dummy variables, one for
each month following the first policy change (August 1965). T x M are
interaction dummies denoting the treatment group membership in months
following the policy changes, and [epsilon] is an error term. In the
aforementioned model, the estimated [delta]s on months 9 and 10 after
each policy change are the difference-in-differences estimates of
interest.
[FIGURE 2 OMITTED]
III. RESULTS
A. Descriptive Analysis
Figure 2 plots the proportions of first births for American women
aged 20-24 yr and 25-29 yr by month and year of delivery. From 1963 to
1968, the two ratios grew about linearly with only small deviations from
the trend. The series, however, exhibited a spike in the summer of
1966--approximately 9 mo after the new draft policies were announced. As
hypothesized, the spike was more remarkable for the younger cohort.
Based on the descriptive analysis, it seems reasonable to focus on
the relatively stable period from January 1963 to December 1968 when
estimating the effects of the new draft policy on fertility. This time
period includes several years preceding the Executive Order 11241
issuance (pre-August 1965) as well as several years following the
expected effects of the new policies on fertility (post-July/August
1966). Limiting the period studied to the mid-1960s also simplifies the
analysis by avoiding the substantial changes to the draft process
associated with the introduction of the draft lottery in late 1969. (6)
Finally, a relatively short follow-up is sufficient for studying the
immediate decision of affected young couples to conceive a first-born
child. Due to the construction of the outcome measure the proportion of
first births to the total number of births--investigating long-term
fertility dynamics would be complicated as the corrective decrease in
the number of first deliveries and an increase in the number of second
and subsequent deliveries would be difficult to separate out. For the
purposes of this study, year 1968 therefore seems like a reasonable
cutoff. Unfortunately, limiting attention to years prior to 1969
excludes the effects of the family deferment elimination of April 1970
from the analysis.
[FIGURE 3 OMITTED]
Since the two series of the first birth ratio likely followed a
different (linear) time trend in 1963-1968 and since their seasonal
pattern might have also differed, appropriate detrending and
deseasonalizing had to be performed. A continuous time variable and a
full set of month dummies have been used. This approach is similar to
that in Card and Lemieux (2001, 2002), who regress the annual education
outcomes on a linear intercohort time trend when estimating the effects
of the Vietnam draft on college attendance.
A simple visual examination of the detrended and deseasonalized
series (Figure 3) suggests that the government draft policies very
likely did have a significant impact on the fertility of the potential
draftees. In particular, while the residual ratios for the treatment and
control groups followed a similar time path in the years 1963-1965, the
treatment mothers experienced a much sharper increase in the proportion
of first births in the summer of 1966. That the control mothers
experienced any increase at all may stem from the fact that maternal age
is an imperfect proxy for paternal age and so that some of the women in
the control group might have also reacted to the draft. As further
obvious from Figure 3, the two cohorts of mothers behaved somewhat
differently toward the end of the studied period. More specifically, the
treatment mothers had a lower residual ratio of first-born babies about
12 and 22 mo after the 1966 spike. This is consistent with the fertility
behavior (birth spacing in particular) prevalent in the United States at
that time. Based on data from the Natality Detail Files for the years
1969-1971, (7) the distribution of the length of time between the first
and the second live birth peaked at months 13 and 23 in the late 1960s
and early 1970s (Figure 4). A decreased number of first births coupled
with an increased number of subsequent births in the years 1967 and 1968
by women who had responded to the Vietnam draft by advancing their first
delivery to summer 1966 may thus be responsible for the observed
pattern.
[FIGURE 4 OMITTED]
B. Regression Results
To formally estimate the size and significance of the effect of the
Vietnam draft rules on natality, I employ a difference-in-differences
type of methodology. In the baseline specification of my model, I
regress the detrended and deseasonalized first-born infants-to-all
infants ratio on a dummy variable set equal to 1 for the treatment
group, seven dummy variables set equal to 1 for months 8-14 after the
August 1965 Executive Order issuance (i.e., months 6-12 after the
October 1965 Selective Service announcement), and seven interaction
dummies set equal to 1 for observations on the treatment group in the
exposed months. (8) If the new policies did induce young women to time
the conception of their first-born child in order to make the
baby's father exempt from the draft, the coefficients on the
interaction dummies for months 9 and 10 after each of the new policies
was announced should be positive and statistically significant. In
addition, since the announcements were made on August 26 and October 26,
1965, even a quick response by the potential draftees would likely
increase the number of infants born in June 1966 (10 mo after the
Executive Order issuance) and August 1966 (10 mo after the Selective
Service announcement) by more than the number of infants born in May and
July 1966. Therefore, the coefficients on the interaction dummies for
months 10 and 12 after the Executive Order issuance (i.e., months 8 and
10 after the October 1965 Selective Service announcement) should be
larger in magnitude.
Results from my baseline ordinary least squares estimation are
reported in the first column of Table 3. Two of the interaction
variables are positive and significant at the 95% confidence level: the
interaction dummies for months 10 and 12 after the Executive Order
issuance, that is, months 8 and 10 after the Selective Service
announcement. The increased natality in June 1966 very likely represents
a direct response to the Executive Order issuance, and the increased
natality in August 1966 is likely caused by the Selective Service
announcement. Even though statistically insignificant, the proportions
of first births among treatment women are higher in July, September, and
October 1966 as well and the gap diminishes over time.
The second column of Table 3 reports results from a specification
where teenagers (mothers aged 15-19 yr) are added to the treatment
group. In this case, the interaction dummies for June, July, August, and
September 1966 are all positive, large, and statistically significant.
Taken together, the aforementioned results thus provide strongly
suggestive evidence that the Vietnam War draft policy played a role in
determining the timing, and perhaps the number, of births.
C. Correction for Misclassification
After estimating the baseline model, I explicitly acknowledge that
some women might have been misclassified into the treatment and/or the
control group. A recent article (Lewbel 2003) demonstrates that as long
as the misclassification probabilities are known to the researcher
(e.g., from a validation sample or from aggregate population
proportions), the true average treatment effect can be calculated as:
[[tau].sup.*] = [tau]/([P.sub.0] + [P.sub.1] - 1), where [tau] denotes
the estimated (biased) treatment effect, [p.sub.0] is the proportion of
untreated individuals in the control group, [p.sub.1] the proportion of
truly treated individuals in the treatment group, and [p.sub.0] +
[p.sub.1] > 1. (The Technical Appendix includes a more extensive
discussion of this result and its use in adjusting my estimates.) As
obvious from the aforementioned formula, the true treatment effect is
zero if and only if the estimated treatment effect is zero. Furthermore,
any misclassification into the treatment and/or the control group will
bias the estimated treatment effect downward. Therefore, my estimates of
the effect of the deferment rules on natality are conservative. If, for
example, 65% of women in the baseline treatment group and 11% of women
in the control group had babies with men of the draft-eligible age (as
suggested by the Natality Detail File estimates), the correct magnitude
of the baseline coefficients on the interaction dummies for months 10
and 12 after the Executive Order issuance (i.e., months 8 and 10 after
the Selective Service announcement) would be nearly double (.016/(.89 +
.65 - 1) = .030 and .017/ (.89 + .65 - 1) = .031, respectively).
Similarly, in the specification where teenagers are added to the
treatment group, the corrected statistically significant coefficients
(months 10-13 after the Executive Order issuance) would be .040, .025,
.037, and .026, respectively.
To attach meaning to these estimates, I calculate the predicted
increase in the number of births. First, I consider the baseline case
with no correction for misclassification. Using the actual number of
deliveries obtained from the Vital Statistics suggests that the number
of first births increased by 6,488 as a result of the new draft policy
announcements. (9) Next, using the corrected treatment effects and
recognizing that 65% of mothers aged 20-24 yr and 11% of mothers aged
25-29 yr were "at risk" modifies the estimate to 8,283. And,
finally, using the baseline estimates but taking into account that a
fraction of the teenage group could have been affected by the new draft
policies further increases the predicted effect to 15,532.
When teenagers are directly added to the treatment group, the
magnitude of the estimated effect increases further. In particular, my
results indicate that the number of first births might have increased by
as many as 19,540 in June and August 1966. In fact, when all the
statistically significant coefficients from the alternative
specification are employed, the predicted number of additional first
births delivered between June and September 1966 rises to 32,914.
D. Robustness Checks
To check the robustness of the baseline results, several
alternative specifications of the difference-in-differences model are
estimated. (10) First, I add dummy variables for all the remaining
months after the Executive Order issuance as well as their interactions
with the treatment dummy to the baseline regression. This way, the
Executive Order of August 1965 and the Selective Service announcement of
October 1965 are allowed to have an effect on fertility throughout the
entire period from September 1965 to December 1968. Results from this
specification are very similar to those reported in the first column of
Table 3.
Next, I consider the possibility that the trend in the first-born
infants-to-all infants ratio was not linear (for either the treatment or
the control cohort) in the mid-1960s. To allow for this possibility, I
follow Card and Lemieux (2001, 2002) and add a quadratic time variable
to the simple linear time term and the full set of month dummies when
detrending and deseasonalizing the original series. I then use the
residuals from this analysis in the difference-in-differences type of
model. The magnitude of the coefficients on the interaction dummies of
interest (10 mo after each of the policy changes) decreases only very
slightly, and both variables remain highly statistically significant.
None of the other interaction dummies reaches statistical significance
at the 95% confidence level. As before, the main conclusions do not
change when the full model (with dummies for all months after September
1965) is estimated.
To verify the causality of the relationship, I also estimate the
aforementioned models for a counterfactual--an artificial (i.e.,
unreal)-policy change. In particular, I assume that instead of being
announced in the summer of 1965, the new draft rules were announced,
alternatively, in the summers of 1962, 1963, 1964, 1966, or 1967. As
hypothesized, the policy coefficients of interest never approach
statistical significance in these models.
Further, to verify that the number of subsequent births is not
driving my results, I use the number of subsequent births instead of the
first-born infants-to-all infants ratio as the dependent variable. As
expected, there is no difference between the treatment and the control
groups of mothers following the policy changes.
Also, since the use of the first-born infants-to-all infants ratio
imposes a functional restriction on the model, I replace this variable
with the number of first birth and add the number of subsequent births
as well as its interaction with the treatment group membership on the
right-hand side (Table 4; note that the number of all births cannot be
used due to endogeneity). Both of the new regressors are positive and
highly statistically significant, but the main results remain
qualitatively the same. The magnitude of the estimates is very similar
as well. In particular, the new results indicate that the number of
first births increased by 2,576 and 3,759 in June and August 1965,
respectively. The sum of these two effects, that is, 6,355 additional
first births, is very close to the 6,488 additional births predicted by
the baseline model (without correction for misclassification). (11)
Finally, in order to formally test the joint hypothesis that the
proportion of first births increased significantly in months 9 and 10
after each of the policy changes, I replace the individual dummies for
months 9-12 after the Executive Order issuance (i.e., months 7-10 after
the October 1965 Selective Service announcement) by a single dummy
variable. As expected, the coefficient on this variable that interacted
with the treatment group membership is large and highly statistically
significant ([??] = .010, SE = .004 for the baseline treatment group and
[??] = .017, SE = .004 for the treatment group including teenagers).
Other coefficients in the model are unaffected by this change.
IV. CONCLUSIONS
The magnitude of the effect of the Vietnam War paternity deferments
on the decision to start a family estimated in this article is quite
substantial. In particular, the calculated conservative increase in the
number of first births by 15,532 in June and August 1966 represents more
than 7% of the total number of first deliveries in those 2 mo. It also
corresponds to about 28% of the Selective Service System calls for
inductees in those months (The Selective Service System 1968). This
finding adds to a growing body of evidence that government interventions
may indeed affect individuals' reproductive behavior. It also adds
to the list of potentially long-lasting effects of the Vietnam War draft
policies.
How does this effect compare to the effects of monetary child
benefits? A good comparator is provided by Milligan (2005) who studies
the fertility effects of the Allowance for Newborn Children (ANC)
implemented between 1988 and 1997 in Quebec. Milligan's results
seem particularly relevant because the ANC, like the paternity
deferments studied here but unlike tax incentives and welfare benefits
studied elsewhere, provided a universal child benefit independent of
income but dependent on the number of previously born children. Also,
Milligan (2005) finds a greater fertility responsiveness to financial
incentives than Aid to Families with Dependent Children studies and so
allows for a conservative estimate of the relative effect of paternity
deferments compared to monetary child benefits.
In Milligan (2005), a newborn lump sum benefit of C$1,000 increases
the probability that a childless woman of reproductive age will have a
first child by 24.3%. In 1966, there were 1,007,324 first births to 15-
to 24-yr-old women in the United States. As calculated in this study, at
least 15,532 of those births are attributable to the paternity
deferments, representing an increase of 1.6%. Using Milligan's
results, the same effect could be achieved by paying (C$1,000 x 1.6/24.3
=) C$66 per child or more than C$66 million for all the 1,007,324 first
children born to mothers aged 15-24 yr in 1966. Using year 1995 exchange
rate of C$1.37 for US$1.00 suggested in Milligan (2005) and converting
to 2006 dollars, the payment required to produce the same increase in
births as that attributable to the Vietnam War paternity deferments
would be US$64 million.
An interesting question that remains is to what extent the increase
in the number of births in the summer of 1966 translated into an
increase in completed fertility and to what extent it represented a mere
change in birth timing. Unfortunately, this issue is difficult to
address with existing data. In an attempt to study subsequent fertility
of women affected by the Vietnam draft, I have examined a sample from
the 5% Public-Use Microdata Sample (PUMS) from the 1980 U.S. Census.
Women who were 20-24 yr old in summer 1966 were 33-37 yr old on the
Census Day of April 1, 1980. I have created a subset of this group
consisting of women who were "householders" or
"spouses" in a family or "spouses" or
"parents" in a subfamily where a child born between April and
September (Quarters 2 and 3) 1966 was present. (12) Since these children
were 13 yr old on the Census Day, they were still likely to be residing
with their parents and so recorded in the PUMS data set. As defined in
the 1980 Census, a "child" refers to an own child, an adopted
child, or a stepchild. Therefore, I have limited my study group to women
who had also had at least one previous birth. This left 30,869 women in
the study group and 365,884 women in the comparison group.
A problem with comparing fertility behavior of women who had a
child in spring or summer 1966 with their same-age counterparts who did
not have a child in this period is that women who chose to become
pregnant at ages 20-24 are likely to differ systematically from other
women in a way which affects their subsequent fertility behavior.
Indeed, as my data show, women who had started with childbearing early
in life had higher fertility by ages 33-37 than women in the comparison
group (3.2 vs. 2.1 children, respectively). To mitigate this problem, I
have selected a "straw man" group from my sample and examined
completed fertility of 33- to 37-yr-old women who had conceived before
the new deferment policies were announced and had a child in January to
March (Quarter 1) 1966. As expected, these 13,744 women were slightly
older than those delivering in April to September 1966 (35.13 vs. 35.09
yr), were more likely to be black (14.4% vs. 12.5%), and less likely to
have completed high school (71.5% vs. 73.6%). However, the mean
fertility of both groups was 3.2 children, and even when controlling for
age, race, and high school education, there was no statistical
difference. So women who had a child in January to September 1966
clearly differ from their counterparts who did not have a child in this
period, but I could not detect any difference between women who were
potentially affected by the new deferment policies and those who were
not. While this could theoretically mean that women reacting to the
policies adopted fertility behavior of those choosing to start
childbearing at a young age, it more likely reflects the fact that the
fraction of affected women in the study group is very small. In
particular, the 30,869 study women in the PUMS data represent 617,380
American women. Since the predicted increase of 15,532 births attributed
to the paternity deferments in this article corresponds to only 2.5% of
the overall population, it is unlikely that a cohort analysis would
reveal significant differences even if they existed.
The Census analysis has a couple of additional limitations. First,
I could not distinguish between own children and adopted children or
stepchildren. Second, not all the children used to construct the study
sample were necessarily first-born children. Unfortunately, older
children might have already left the household (and the data set).
Third, the PUMS data only report the quarter--not the month--of birth.
As a result, the window of April to September 1966 is wider than the
period in which the effects of the paternity deferments were
concentrated (i.e., June to August 1966). These problems can be avoided
by examining the Current Population Survey 1995 Fertility and Marital
History Supplement. From this data set, I obtained the distribution of
the lifetime number of births (completed fertility) for women aged 20-24
yr at their first delivery whose first child was born in the summer of
1966. I then compared this distribution to the corresponding
distributions for women whose first delivery occurred in the summers of
1962 1965 and 1967-1970. Unfortunately, the number of observations
(about 80 each year--753 in total) was too low to enable reliable
comparisons. Furthermore, the methodology used here and in the Census
analysis mentioned previously made it impossible to study the proportion
of women with no births. This is an important limitation since, as
Ananat, Gruber, and Levine (2004) note, zero is the only point in the
fertility distribution for which there is an unambiguous prediction: in
the case examined here, the proportion of childless women should fall.
Following Ananat, Gruber, and Levine (2004), I have therefore considered
a complementary approach. In particular, I have used the method of
cohort analysis to study completed fertility of women aged 10-14 yr,
15-19 yr, 20-24 yr (the exposed group), 25-29 yr, and 30-34 yr in the
year 1966. For the purposes at hand, however, this analysis proved too
crude as the general decline in fertility over time strongly dominated
any other fertility pattern.
While it is not clear whether the paternity deferments affected
completed fertility or the timing of birth, the consequences of either
change--in terms of maternal education, labor market behavior, marital
decisions, maternal and child health, and other outcomes--could be
important. For example, Rosenzweig and Schultz (1985) demonstrate that
the effects of family size on female labor market outcomes can be
significant. Angrist and Evans (1998) corroborate this finding and show
that fertility reduces female labor supply especially among poor and
less educated women. Moreover, previous literature indicates that
circumstances surrounding first birth are specifically important. For
example, using the National Longitudinal Survey, Shapiro and Mott (1994)
show that the employment behavior surrounding first births in 1968-1973
is an important independent predictor of female lifetime work
experience. Jacobsen, Pearce, and Rosenbloom (1999) use the 1970 and
1980 U.S. Census data on married nulliparous women who gave birth to
twins. Using the twin child as an unplanned additional birth, they find
that unplanned first births reduce female labor supply and earnings.
Focusing on the consequences of teenage pregnancy, McElroy (1996)
finds that having a birth as a teenager reduces the likelihood of high
school completion and college enrollment even after controlling for
observable factors that account for the lower socioeconomic status of
teenage mothers during their childhood. Hotz, McElroy, and Sanders (2005) use miscarriages as an instrument to better control for the
endogeneity of having a birth as a teenager. They conclude that early
childbearing does decrease high school completion, but the effect is
smaller than previously believed.
With respect to the timing of birth and health, Royer (2004)
investigates the effects of maternal age on birth outcomes. Comparing
outcomes across siblings born in Texas between 1989 and 2001, she
concludes that "the 'best' age for first and second
births is between 22 and 25" (p. 24) and that younger and older
mothers face an elevated risk of pre-term delivery, infant death, and
child's abnormal condition. Thus, 20- to 24-yr-old women are at an
ideal age for childbearing, but to the extent the paternity deferments
induced births among teenagers, they might have had a detrimental effect
on infant health. Overall, the indirect evidence available suggests that
by influencing natality, the draft deferments likely had other
long-lasting effects.
ABBREVIATIONS
ANC: Allowance for Newborn Children
NLSYM: National Longitudinal Survey of Young Men
PUMS: Public-Use Microdata Sample
TECHNICAL APPENDIX: ESTIMATION OF AVERAGE TREATMENT EFFECTS WITH
MISCLASSIFICATION
Based on Lewbel, A. "Estimation of Average Treatment Effects
with Misclassification," Working Paper, 2003 (especially
"Identification by Known Misclassification Probabilities," pp.
5-8, and "Proof of Theorem 1," pp. 24-5).
http://www2.bc.edu/~lewbel/mistrea11.pdf.
Notation
Y, Observed outcome
[T.sup.*], Actual treatment
T, Reported treatment
t = 1, Receiving treatment
t = 0, No treatment
Y(t), Outcome from treatment [T.sup.*] = t
X, Vector of observable covariates
[ILLUSTRATION OMITTED]
Definitions
[p.sub.0](x) = E[Z([T.sup.*] = 0)|x = x, r = 0] = O/(C + D) =
D/T2(= .89)
[p.sub.1](x) = E[I([T.sup.*] - 1)|X = x, T = 1] = A/(A +B) = A/TI(=
.65)
[right arrow] The relative sizes of groups "T = 1" and
"T = 0" do not matter for the calculation of [P.sub.0](x) and
[p.sub.1](x).
[b.sub.0](x) = E[I(T = I)|X = x, [T.sup.*] 0] - B/(B + D)
[b.sub.1](x) - E[I(T - 0)|X - x, [T.sup.*] = 1] = C/(A + C)
[right arrow], The relative sizes of groups "T = 1" and
"T = 0" do matter for the calculation of [b.sub.0](x) and
[b.sub.1](x)
[r.sup.*](x) = E[[T.sup.*]|X = x]
[[h.sup.*.sub.t](x) = E[Y|X = x, [T.sup.*] = t] = (from assumption
#2 below)E[Y|X = x, [T.sup.*] = t,T]
[[tau].sup.*](x) = E[Y|X : x, [T.sup.*] = 11 - E[Y|X = x, [r.sup.*]
= 0] = [h.sup.*.sub.1](x) - [h.sup.*.sub.0](x) = (from assumption #1
below)E[Y(1) -(x) Y(0)|X = x] [right arrow] the average treatment effect
[tau](x) = E[Y|X = x, T = 1] - E[Y|X = x, T = 01
Assumptions (pp. 5-7 in Lewbel 2003)
1. Unconfoundedness: E[Y(t)|[T.sup.*], X] = E[Y(t)|X] [right arrow]
treatment group membership has no effect on outcomes other than through
the effects of treatment itself [right arrow] O.K.
2. E[Y|X, [T.sup.*], T] = E[Y|X, [T.sup.*]] [right arrow]
assignment into the treatment group has no effect on outcomes when true
treatment group membership is controlled for [right arrow] O.K.
3. i) [b.sub.0](x)+[b.sub.1](x)<1([b.sub.0](x)+[b.sub.1](X)=0.35
x T1/(0.35 x T1 +0.89 x T2)+0.11 x T2/(0.11T2+0.65T1) = (0.0385 x T1 x
T2+0.2275 x [T1.sup.2]+0.0385 x T1 x T2+[0.0979T2.sup.2])/ (0.0385 x T1
x T2+0.2275 x [T1.sup.2]+0.5785 x T1 x T2+ [0.0979T2.sup.2]) < 1)
[right arrow] O.K.
ii) E[[T.sup.*] |X = x, T = 1] [not equal to] E[[T.sup.*] |X = x, Y
= 0] (E[[T.sup.*] |X = x, T = 1] = 0.65 [not equal to] E[[T.sup.*]|X =
x, T = 0] = 0.11) [right arrow] O.K.
iii) 0 < [r.sup.*](x)<1[r.sup.*](x) = (A + C)/(A + B+C + D)
[right arrow] O.K.
4. [tau](x) is identified, i.e., consistently estimated
Derivation (pp. 24-5 in Lewbel 2003)
[MATHEMATICAL EXPRESSION NOT REPRODUCIBLE IN ASCII]
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(1.) Unfortunately, only a few transcripts of television news are
available for years prior to 1968 (Vanderbilt Television News Archive,
NBC News Archive, and Burrell's Transcript Service), and none of
them is relevant to the issue at hand.
(2.) I have explored several micro data sets, but none of them was
suitable for this study. For example, the Natality Detail File series
only started in the year 1968. The Current Population Survey reports age
in years but not the month of birth (making it impossible to focus on
children as respondents) and only asks females questions related to
fertility (making it impossible to link children to their fathers and to
focus on fathers as respondents). The National Longitudinal Survey of
Young Men (NLSYM) includes information on individuals 14-24 yr old in
the year 1966 but contains no appropriate control group. Also, the
sample size in the NLSYM is too small to permit reliable inferences from
a stratified analysis (e.g., in the summer of 1966, sampled men aged
19-24 yr old had only 22 first-born children). The Childbirth and
Adoption History File of the Panel Study of Income Dynamics collected
since 1985 does not contain enough first births in the control group to
support reliable difference-in-differences estimation.
(3.) Source: http://www.cdc.gov/nchs/data/statab/t941x 18.pdf,
http://www.cdc.gov/nchs/data/statab/t941x19.pdf,
http://www.cdc.gov/nchs/data/statab/t941x07.pdf, and http://
www.census.gov/popest/archives/pre- 1980/PE-11.html [accessed March 19,
2006].
(4.) These are the first years when the age of both parents was
recorded.
(5.) At its peak in April 1969, the U.S. participation in Vietnam
involved 543,000 troops (http://www.history. navy.mil/wars/foabroad.htm
[accessed July 23, 2007]).
(6.) Beginning in 1970, young men were at risk of induction for
only 1 yr rather than for the entire period between ages 18.5 and 25, as
was the case previously. As Card and Lemieux (2001, 2002) note, the
shortened period of exposure together with the relatively low rate of
inductions after 1969 significantly reduced the incentives to pursue
draft-avoidance strategies.
(7.) These are the first years when the information on birth
spacing was recorded by at least some states. Obtaining this information
for the years 1966-1968 would have been preferable since, if the number
of first births was exogenously affected by the policy change, birth
spacing might have been affected as well. Nevertheless, the stability of
the birth spacing distribution in the 1969-1971 period makes
extrapolation to the earlier years seem justifiable.
(8.) As a robustness check, I have also estimated the main equation
with detrending and deseasonalizing in one step. This modification had
no substantial impact on the results.
(9.) Let [Y.sub.1] denote the number of first births, [Y.sub.2] the
number of subsequent births, and Z the policy change of interest. Then,
[tau] - [partial derivative][[Y.sub.1]/([Y.sub.1] + [Y.sub.2])]/[partial
derivative]Z = [([partial derivative][Y.sub.1]/[partial derivative]Z) x
([Y.sub.1] + [Y.sub.2]) - [Y.sub.1] x ([partial
derivative][Y.sub.1]/[partial derivative]Z + [partial
derivative][Y.sub.2]/[partial derivative]Z)]/[([Y.sub.1] +
[Y.sub.2]).sup.2], where [partial derivative][Y.sub.2]/[partial
derivative]Z is assumed to be 0 (this assumption is verified in my
analysis of subsequent births). Thus, [partial
derivative][Y.sub.1]/[partial derivative]Z = [[tau].sup.*][([Y.sub.1] +
[Y.sub.2].sup.2]/[Y.sub.2]. Using the actual numbers of first and
subsequent births to women aged 20-24 yr reported in the Vital
Statistics yields: [partial derivative][Y.sub.1]/[partial derivative]Z =
(.016 x [107,042.sup.2]/61,796 =) 2,967 (June 1966) + (.017 x
[116,886.sup.2]/65,966 =) 3,521 (August 1966) = 6,488.
(10.) Results from all alternative estimations are available upon
request.
(11.) I have also considered using a birth rate as the dependent
variable. Unfortunately, monthly population estimates for the 1960s are
not available (U.S. Census Bureau). Therefore, a birth rate would need
to use annual population estimates in the denominator. Since the effects
of the paternity deferment policies seem to be month
specific--concentrated 10 mo after their enactment--adding annual
population estimates to the dependent variable would not contribute to
the estimation of this 10-mo lag.
(12.) This method of matching children with mothers is similar to
Angrist and Evans (1998).
ANDREA KUTINOVA, I am indebted to Karen Conway, Robert Mohr, Partha
Deb, Reagan Baughman, Robert Woodward, and seminar participants at the
University of New Hampshire for very helpful suggestions and comments.
Kutinova: Lecturer, Department of Economics, University of
Canterbury, Private Bag 4800, Christchurch, New Zealand. Phone (3) 364
2823, Fax (3) 364 2635, E-mail andrea.kutinova@canterbury.ac.nz
TABLE 1
Median Age of Brides and Grooms at the
Time of First Marriage, United States,
1963-1968
Median Age Median Age Difference in
Year of Brides of Grooms Median Age
1963 20.3 22.5 2.2
1964 20.5 23.0 2.5
1965 20.4 22.5 2.1
1966 20.3 22.6 2.3
1967 20.8 22.9 2.1
1968 20.6 22.4 1.8
Source: National Center for Health Statistics, Centers
for Disease Control and Prevention (1967-1971).
TABLE 2
Percentages of Fathers Aged 19-25 Yr by
Mother's Age, United States, 1969-1971
Year 1969 1970 1971
% Missing information 9.18 9.70 9.89
on father's age
Mother's age cohort
20-24 yr old 64.82 65.10 65.46
(baseline treatment group)
15-24 yr old 68.30 68.33 68.62
(alternative treatment group)
25-29 yr old (control group) 11.18 10.84 11.20
Source: U.S. Department of Health and Human Services,
National Center for Health Statistics (1970-1972).
TABLE 3
The Effects of the Vietnam War Paternity Deferments on the Proportion
of First Births, United States, 1963-1968; Ordinary Least Squares
Estimation
Parameter Estimate
Baseline
Treatment Group
Variable (20-24 Yr Old)
Treatment cohort -0.001 (0.001)
8 mo after the Executive Order 11241 issuance/6 -0.003 (0.006)
mo after the October 1965 Selective Service
announcement
9 mo after the Executive Order 11241 issuance/7 -0.001 (0.006)
mo after the October 1965 Selective Service
announcement
10 mo after the Executive Order 11241 issuance/8 -0.004 (0.006)
mo after the October 1965 Selective Service
announcement
11 mo after the Executive Order 11241 issuance/9 0.004 (0.006)
mo after the October 1965 Selective Service
announcement
12 mo after the Executive Order 11241 issuance/10 0.002 (0.006)
mo after the October 1965 Selective Service
announcement
13 mo after the Executive Order 11241 issuance/11 0.002 (0.006)
mo after the October 1965 Selective Service
announcement
14 mo after the Executive Order 11241 issuance/12 0.007 (0.006)
mo after the October 1965 Selective Service
announcement
8 mo after the Executive Order 11241 issuance/6 -0.003 (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
9 mo after the Executive Order 11241 issuance/7 -0.001 (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
10 mo^ after the Executive Order 11241 issuance/8 0.016 ** (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
11 mo after the Executive Order 112A1 issuance/9 0.007 (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
12 mo after the Executive Order 71241 issuance/10 0.017 ** (0.008)#
mo^ after the October 1965 Selective Service
announcement x treatment cohort#
13 mo after the Executive Order 11241 issuance/11 0.011 (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
14 mo after the Executive Order 11241 issuance/12 0.003 (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
Parameter Estimate
Alternative
Treatment Group
Variable (15-24 Yr Old)
Treatment cohort -0.001 (0.001)
8 mo after the Executive Order 11241 issuance/6 -0.003 (0.005)
mo after the October 1965 Selective Service
announcement
9 mo after the Executive Order 11241 issuance/7 -0.001 (0.005)
mo after the October 1965 Selective Service
announcement
10 mo after the Executive Order 11241 issuance/8 -0.004 (0.005)
mo after the October 1965 Selective Service
announcement
11 mo after the Executive Order 11241 issuance/9 0.004 (0.005)
mo after the October 1965 Selective Service
announcement
12 mo after the Executive Order 11241 issuance/10 0.002 (0.005)
mo after the October 1965 Selective Service
announcement
13 mo after the Executive Order 11241 issuance/11 0.002 (0.005)
mo after the October 1965 Selective Service
announcement
14 mo after the Executive Order 11241 issuance/12 0.007 (0.005)
mo after the October 1965 Selective Service
announcement
8 mo after the Executive Order 11241 issuance/6 0.007 (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
9 mo after the Executive Order 11241 issuance/7 0.011 (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
10 mo^ after the Executive Order 11241 issuance/8 0.023 *** (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
11 mo after the Executive Order 112A1 issuance/9 0.014 * (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
12 mo after the Executive Order 71241 issuance/10 0.021 *** (0.008)#
mo^ after the October 1965 Selective Service
announcement x treatment cohort#
13 mo after the Executive Order 11241 issuance/11 0.015 ** (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
14 mo after the Executive Order 11241 issuance/12 0.005 (0.008)#
mo after the October 1965 Selective Service
announcement x treatment cohort#
Notes: The dependent variable is the linearly detrended and
deseasonalized proportion of first births to all U.S. births (144
observations). An intercept term (not statistically significant) was
included in the model. Standard errors are given in parentheses.
Shaded cells highlight the interacted variables (i.e., [T.sub.j] x
[M.sub.t]) and their coefficients (i.e., [delta]). Ten months after
the studied policy changes are indicated in bold.
*** Statistical significance at the 99% confidence level; **
statistical significance at the 95% confidence level; * statistical
significance at the 90% confidence level.
Note: Shaded cells highlight the interacted variables (i.e., [T.sub.j]
x [M.sub.t]) and their coefficients (i.e., [delta]) are indicated with
#.
Note: Ten months after the studied policy changes are indicated with
^.
TABLE 4
The Effects of the Vietnam War Paternity Deferments on the Number
of First Births, United States, 1963-1968; Ordinary Least Squares
Estimation
Parameter Estimate,
Baseline Treatment
Variable Group (20-24 Yr Old)
Treatment cohort 455.19 (6,423.44)
Number of subsequent births 0.31 *** (0.05)
Number of subsequent births x treatment 0.35 *** (0.09)
cohort
8 mo after the Executive Order 11241 -20.28 (950.42)
issuance/6 mo after the October 1965
Selective Service announcement
9 mo after the Executive Order 11241 419.63 (978.87)
issuance/7 mo after the October 1965
Selective Service announcement
10 mo after the Executive Order 11241 140.84 (969.92)
issuance/8 mo after the October 1965
Selective Service announcement
11 mo after the Executive Order 11241 1,358.64 (1,015.25)
issuance/9 mo after the October 1965
Selective Service announcement
12 mo after the Executive Order 11241 862.29 (982.75)
issuance/10 mo after the October 1965
Selective Service announcement
13 mo after the Executive Order 11241 841.22 (976.81)
issuance/11 mo after the October 1965
Selective Service announcement
14 mo after the Executive Order 11241 1,357.21 (978.84)
issuance/12 mo after the October 1965
Selective Service announcement
8 mo after the Executive Order 11241 -1,256.40 (1.344.63)#
issuance/6 mo after the October 1465
Selective Service announcement x
treatment cohort#
9 mo after the Executive Order 11241 -966.06 (1,379.01)#
issuance/7 mo after the October 1965
Selective Service announcement x
treatment cohort#
10 mo^ after the Executive Order 11241 2,576.34 * (1,391.64)#
issuance/8 mo after the October 1965
Selective Service announcement x
treatment cohort#
11 mo after the Executive Order 11241 1,476.56 (1,446.25)#
issuance/9 mo after the October 1965
Selective Service announcement x
treatment cohort#
12 mo after the Executive Order 11241 3,758.99 *** (1,407.67)#
issuance/10 mo^ after the October 1965
Selective Service announcement x
treatment cohort#
13 mo after the Executive Order 11241 2,430.89 * (1,382.85)#
issuance/11 mo after the October 1965
Selective Service announcement x
treatment cohort#
14 mo after the Executive Order 11241 1,134.80 (1,372.37)#
issuance/12 mo after the October 1965
Selective Service announcement x
treatment cohort#
Notes: The dependent variable is the linearly detrended and
deseasonalized number of first U.S. births (144 observations).
An intercept term was included in the model. Standard errors are
given in parentheses. Shaded cells highlight the interacted
variables (i.e., [T.sub.j] x [M.sub.t]) and their coefficients
(i.e., [delta]). Ten months after the studied policy changes are
indicated in bold.
*** Statistical significance at the 99%, confidence level;
* statistical significance at the 90% confidence level.
Note: Shaded cells highlight the interacted variables (i.e.,
[T.sub.j] x [M.sub.t]) and their coefficients (i.e., [delta])
are indicated with #.
Note: Ten months after the studied policy changes are indicated
with ^.
