Does Parental Consent for Birth Control affect Underage Pregnancy Rates? The case
of Texas
November 2011
Preliminary version: comments are most welcome, but please do not cite without permission.
Sourafel Girma
School of Economics
Sir Clive Granger Building
Nottingham University
University Park
Nottingham
NG7 2RD
United Kingdom
Tel: + 00 44 115 951 5482
Email: Sourafel.Girma@nottingham.ac.uk
and
David Paton*
Nottingham University Business School
Jubilee Campus
Wollaton Road
Nottingham
NG8 1BB
United Kingdom
Tel: + 00 44 115 846 6601
Email: David.Paton@nottingham.ac.uk
*Corresponding author
Acknowledgements:
We are very grateful to Janice Jackson at the Texas Department of State Health Services for
her assistance with the birth and abortion data. We thank also participants at a staff seminar
at the University of Surrey for useful comments.
Does Parental Consent for Birth Control affect Underage Pregnancy Rates? The case
of Texas
Abstract
In 2003, Texas became the second state to mandate parental consent for the provision of
state-funded contraception to minors. Previous work based on conjectural responses of
minors, predicted that the ruling would lead to a large increase in the Texas underage
pregnancy rate. In this paper we examine the actual impact of the parental consent mandate
on the under-18 pregnancy rate using both state- and county-level data and using 18-year olds
as a control group. The county-level data allows us to use a statistical matching estimator to
compare the effect of parental consent in counties with and without family planning clinics
that are subject to the ruling. We control for both observable and unobservable
characteristics that may be systematically correlated with the presence of affected clinics by
combining difference-in-differences and difference-in-difference-in-differences strategies
with propensity-score weighted regressions. The estimates provide little evidence that
requiring parental consent for state-funded contraception led to an increase in the underage
pregnancy rate.
Keywords: propensity score weights; parental consent; family planning; teenage pregnancy;
abortion.
JEL Classifications: C21, I18, J13.
2
Does Parental Consent for Birth Control affect Underage Pregnancy Rates? The case
of Texas
1. Introduction
In this paper we use treatment effects evaluation estimators to test whether mandatory
parental consent for the provision of state-funded birth control to minors leads to an increase
in underage pregnancies. Policy discussions on the appropriate level of parental involvement
in sexual health decisions of minors generate a huge amount of controversy. The underlying
ethical debate rests on the balance between the rights of minors to make autonomous
healthcare decisions and the rights of parents and carers to be involved in decisions affecting
those for whom they have legal responsibility. In practice, policy arguments often hinge on
the likely impact of mandatory parental involvement on the sexual health of minors and, in
particular, rates of underage pregnancy.
Legislation to mandate parental involvement for birth control in the U.S. has been
considered recently both at the federal level and by numerous state legislatures. Other
countries such as England, the Republic of Ireland and the Philippines are in the process of
debating proposals either to abolish existing parental consent provisions for contraception or
to put new ones in place. Despite the level of activity in the policy arena, the academic
literature has paid very little attention indeed to this issue. This is in stark contrast to the
considerable body of evidence, much of it conducted by economists, relating to parental
involvement for abortion.
In January 2003, Texas became the second U.S. jurisdiction to mandate parental
consent for the provision of state-funded contraception to teenagers below the age of 18.1
Franzini et al (2004) use survey data on conjectural responses of teenagers to changes in
confidentiality along with data on failure rates of contraception to estimate the likely effect of
the Texas regulations. They projected that the law would lead to more than 5,000 additional
births and 1,600 additional abortions per year amongst minors in the State. This implies an
increase in the underage pregnancy (defined as abortions plus births) rate of about 20%, with
an estimated direct medical cost of about $44 million.
Whether or not these projections translate into actual additional pregnancies and costs
depends on the actual, rather than behavioral, response of minors. To date no research has
been undertaken to estimate the actual effect of the Texas parental consent law on pregnancy
rates amongst minors and it is this gap which we are trying to fill in this paper. The results
1
Utah has had s similar restriction in place for a number of years.
3
are likely to be of interest not only to policymakers in Texas but also to those in other states
and countries which may be considering the introduction of similar laws. Further, the results
should provide insights into whether adolescents respond to new incentives induced by
regulatory change in ways predicted by standard neo-classical models.
The empirical approach taken in the paper is first to undertake some preliminary
analysis to explore whether the parental consent law for family planning actually affected the
take-up of contraception amongst adolescents. We then test for a state-wide effect of parental
consent on pregnancy by comparing changes in rates amongst minors before and after the
ruling relative to changes amongst older teenagers.
Establishing a causal effect at the state level is potentially complicated by state-wide
changes to minor pregnancy rates caused by other contemporaneous factors. For example, in
September 2005, Texas strengthened its parental involvement law for abortions on minors,
mandating parental consent rather than just notification. To control for such effects, we
exploit the fact that parental consent for contraception is only required for state-funded, rather
than federally-funded, contraception. That means that family planning clinics receiving
funding under the (federal) Title X scheme, should be relatively unaffected by the ruling,
whilst non-Title X funded clinics will be affected. By identifying those counties with such
affected clinics, we are able to use statistical matching methods to help isolate any causal
effect of the parental consent mandate. We are careful to control for both observable and
unobservable characteristics that may be systematically correlated with the presence of
affected (i.e. non-Title X) clinics. We do so by combining, difference-in-differences and
difference-in-difference-in-differences strategies with propensity-score weighted regressions.
2. Parental Consent for contraception – the evidence to date
Following the seminal work of Becker (1963), the economic literature has offered several
theoretical models in which teenagers make decisions regarding sexual activity, contraceptive
use and pregnancy resolution based on their subjective evaluation of expected costs and
benefits of uncertain outcomes. Akerlof, Yellen and Katz (1996) and Paton (2002) argue that
easier access to contraception may lower the perceived costs of underage or extra-marital
sexual activity and, as a result, can have an ambiguous effect on unwanted pregnancy or
abortion rates. Similar models have been presented in the context of sex education
(Oettinger, 1999) and abortion (Levine, 2003, 2004). More recently, Arcidiacono, Khwaja
and Ouyang (2011) develop an inter-temporal model in which “habit persistence” is a feature
of teen sexual behavior. Once a relationship progresses to sexual intercourse, the authors
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argue that it becomes harder for the couple to switch back to abstinence. The prediction,
confirmed in their empirical analysis, is that more costly access to contraception leads to an
increase in teen pregnancies in the short run, but to a decrease in the long run.
In the context of such economic models, the predicted effects of a parental consent
requirement for contraceptives on underage pregnancies are unclear. Such policies might
discourage some young women from having sexual intercourse, which should lead to a
reduction in pregnancies among minors. However, pregnancies could increase if some young
women who would have used prescription contraceptives absent the parental consent policy
have intercourse anyway but use less effective methods of birth control or no contraception at
all. Pregnancies would not be affected if minors, who would have used prescription birth
control absent the policy, either obtain parental consent after the policy change or, instead,
manage to access supplies from other providers.
A number of studies have used surveys to obtain conjectural responses from teenagers
on their likely response to hypothetical parental involvement requirements. These studies
suggest that parental consent laws might indeed affect both teens’ sexual activity and
contraceptive use. In a survey conducted at Planned Parenthood clinics in Wisconsin, 59% of
minors said they would discontinue use of contraceptive services if parental involvement
were required (Reddy, Fleming and Swain, 2002). In surveys conducted at publicly funded
family planning clinics across the U.S., 40% of young women said they would not go to
publicly funded clinics that required parental consent for prescription birth control (Jones et
al., 2005). Some minors said they would switch to condoms or other non-prescription forms
of birth control. About 6% said they would continue to have intercourse but not use any
contraceptives. About 7% said they would stop having intercourse, although only 1%
indicated this as their only likely response. However, 60% of minors in one study (Jones et
al., 2005) and 45% of teens in another (Harper et al., 2004) said a parent was already aware
they obtained sexual health services at a clinic, suggesting that many minors might not
change their behavior in response to a parental consent policy.
The results of these conjectural responses form the basis for the predictions by
Franzini et al (2004) that the parental control mandate in Texas would lead to a large increase
in underage pregnancies. However, it is difficult to assess the actual effect of a parental
involvement requirement from surveys about hypothetical policy changes. Indeed, previous
studies of the impact of more general changes to availability of family planning to minors are
at best inconclusive (Girma and Paton, 2006, 2011; Kearney and Levine, 2009; Raymond et
al., 2007; Evans, Oates and Schwab, 1992).
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In the first place, it may be that teen’s actual responses will be very different to the
hypothetical responses declared to researchers. Second, the samples for such studies tend to
be drawn from teens attending birth control clinics and who are likely already to be sexually
active. The work by Arcidiacono et al (2011) suggests that the response may be very
different amongst young people who are not yet sexually active but who will consider such a
transition in the future.
Very few studies have examined the actual impact of limitations on the confidentiality
for contraception on pregnancy rates (rather than just on the uptake of services). Paton
(2002) examines the impact of the Fraser ruling which meant that for most of 1985, family
planning could not be provided to underage girls without parental involvement in England
and Wales. Take-up at family planning clinics amongst this age group dropped by about 30%
in 1985, yet the underage conception rate in England decreased slightly relative to the rate
amongst older teenagers. Similarly, the rate also did not increase relative to the underage
conception rate in Scotland where the Fraser ruling did not apply.
A previous study of the imposition of parental consent for family planning in a single
county (McHenry) in Illinois found that the requirement led to an increase in the percentage
of births to women under age 19 living in McHenry County relative to three other nearby
counties but not to an increase in the percentage of abortions or pregnancies occurring among
teens (Zavodny, 2004; Zavodny, 2005). To date no studies at all have examined the impact
of the parental involvement restrictions for family planning at a state-wide level.
There does exist a much larger literature on the related issue of parental involvement
for abortion. Methodological difficulties, such as controlling adequately for abortions carried
out in neighboring states without such a law, make it hard to draw firm inferences from the
data, but the majority of studies to date find that parental involvement laws have significant
effects on teenage fertility and sexual behavior. For example, relative decreases in underage
abortion rates are observed by New (2011), Joyce, Kaestner and Colman (2006) and Levine
(2003) whilst the latter also concludes that these laws lead to reduction in total pregnancy
rates amongst minors. Klick and Stratmann (2008) use rates of sexually transmitted
infections (STIs) as a proxy for risky sexual activity and find that states implementing
parental involvement laws experienced relative reductions in some STIs amongst minors.
There is some evidence that parental involvement laws have differential effects for older and
younger teenagers. For example, Colman, Joyce and Kaestner (2008) provide evidence that
the 2000 law mandating parental notification before abortions on minors in Texas decreased
both abortions and births amongst girls aged 17 at the time of the birth or abortion. However,
6
amongst a slightly older cohort (girls aged 17 at the time of conception) abortions decreased
by a lower amount whilst births increased (albeit by a statistically insignificant amount).
3. Methodology
3.1 State-level Estimates
Based on aggregate state level data, we employ logit regression for grouped data to determine
the impacts of the parental consent mandate on underage pregnancy rates. We measure the
impacts as changes from 2002 (the year before the mandate) to the three years after the
mandate for two treatment groups: under-18s (U18) and under-16s (U18), relative to the 18
years olds (the control group).2 The Texas parental consent mandate applies to those aged
under-18. There are several reasons for selecting the second treatment group (under-16s). In
the first place, previous research (Colman et al, 2008) suggests that the impact of parental
consent laws may differ between older and younger teens. One reason for this is that parental
consent may be more strongly binding to younger teens who are less likely to be able to
travel independently to access alternative sources. Further, policy makers tend to be
relatively more concerned about pregnancies amongst younger teens than amongst those
approaching the age of majority. Finally, some older minors (for example those that are
married) are considered ‘emancipated’ in Texas state law and are exempt from the parental
consent ruling.
Since our estimation methodology involves “before” and “after” periods for the
control and treatment groups, the relevant estimates can be interpreted as difference-indifferences estimates. The estimating equation in this analysis can be expressed as:
(1)
where p is the number of pregnancies (abortions plus births) divided by the population for the
relevant age group at the estimated time of conception, i represents the three age groups;
t=2002,….,2005, and Du16 and Du18 denote group dummies for under-16s and under-18s
respectively. We repeat the analysis for the whole sample and for the sample of NonHispanic Whites, Non-Hispanic Blacks and Hispanics separately.
Our results are robust to using more than one year for the “before” period. We also report results for each
individual year of the “after” period.
2
7
3.2 County Level Estimates
The availability of county-level data allows us to estimate the average treatment effect of the
binary treatment, parental consent for family planning, on the scalar outcome variable,
county-level pregnancy rate. Our identification strategy exploits the fact that parental
consent for contraception is only required for state-funded, rather than federally-funded,
contraception. That means that family planning clinics receiving funding under the Title X
scheme, should be relatively unaffected by the ruling compared to non-Title X funded clinics.
In our empirical model we are careful to control for two potential sources of bias: (i)
unobservable characteristics that are correlated with both the treatment and outcome; and (ii)
the possibility that assignment to the treatment is systematically correlated with observable
pre-treatment characteristics, or the self-selection problem.
Following the seminal contribution of Rosenbaum and Rubin (1983), one can remove
estimation bias by using propensity score matching, where the propensity score is defined as
the probability of assignment to the treatment conditional on pre-treatment characteristics,
say Z. More recent work has shown that greater efficiency relative to propensity score
matching can be obtained if one transforms the propensity score estimates into weights in the
relevant regressions, the so-called the propensity score reweighted regression (Hirano et al,
2003 and Busso et al, 2009). In this approach, treatment observations receive a weight of
whereas control observations receive a weight of
,
.
It is worth noting that controlling for self-selection by adjusting for the propensity
score would not remove all biases as long as there are unobservable characteristics affecting
the potential outcomes and the decision to select into treatment. Fortunately, the influence of
time-invariant unobservable characteristics can be controlled by using country-level fixed
effects in the regressions, which is equivalent to using the difference-in-differences (DD)
estimator in a two-period (pre- and post-treatment) panel data model. Hence our baseline
econometric model consists of combining the DD approach with propensity score reweighted
regression. The steps involved in this approach can be summarized as follows:
(i) Estimate the propensity score via a probit model of the probability treatment in 2003
as a function of pre-treatment (2002) characteristics:
. The
characteristics used to obtain the propensity score are as follows: the percentage of the
population living in poverty (poverty); the two-year lagged pregnancy rate (lag
pregnancies); an indicator variable for whether or not the county is urban in nature
(urban); an indicator variable for whether or not the county borders either Mexico or
8
another U.S. state (border); the proportion of the relevant population that are Hispanic
(Hispanic); the proportion of the population that are Black (Black); the number of
Title X (i.e. unaffected) clinics present in the county as of 2001 (Title X (2001)).
Based on the estimated propensity scores, we only keep observations on the common
support by deleting control observations whose propensity score is smaller (higher)
than the minimum (maximum) propensity score of the treatment group.
(ii) Denoting the outcome variable (under-18s/under-16s pregnancy rate) by y, we run the
following propensity-score reweighted DD regressions separately for t=2003, 2004
and 2005:
(2)
In the above equation, the estimate of s is interpreted as the average treatment effect of
Title-X clinic attendance in 2003 on pregnancy rate at time t.
Refining the DD estimator
A key identifying assumption of the DD estimator is the so-called same time-effect condition
which stipulates that, while treated and untreated units may be systematically different in
terms of the level of the response variable y, the trend in y would not have been different
across units in the absence of treatment. The presence of differential trends in the outcome
variable across treated and untreated counties can therefore bias the DD estimator.
To guard against this possibility, we refined Equation (1) by using the more robust
difference-in-difference-in-differences (DDD) strategy. Specifically, we calculate the change
in outcome of the under-18s/under-16s in treatment adopting counties relative to that of the
older cohort (18 year olds) in the same counties, and measure this relative to the equivalent
change in the non-treatment counties. Cast in a regression framework, this translates into
running the following propensity score reweighted regressions
(3)
Exploring heterogeneous treatment effects
As noted earlier, the estimate of the s in the above regressions provides a consistent estimate
of the average treatment effect. The approach we follow can easily be extended to explore
the possibility that the treatment effects depend on pre-sample characteristics by interacting
the treatment dummy with selected demeaned covariates (e.g. Wooldridge, 2002, chapter 18).
Accordingly we also allow the treatment effects of Title-X clinic attendance to vary
9
according to the proportions of blacks and Hispanics in the county population of females
aged 15-19. Denoting these demeaned proportions by X, Equation 2 can be modified as:
(4)
4. Data and Descriptive Statistics
The Texas Department of Health provided data on abortion and births by county of residence
along with estimated gestational age, date of birth of mother. These data enabled us to
estimate ages at conception for all Texas residents including those abortions taking place outof-state. As noted by Joyce et al (2006), the fact that the Texas abortion and birth datasets are
available by year of and age at conception make them far superior to data from many other
states which are only available according to the date of the actual abortion or birth. Having
data by state of residence also gets around the problem that some residents will obtain
abortions (or give birth) in other states. We construct rates of pregnancies for all those under
the age of 18 and also for under-16s on the grounds that the impact of the change may be
different for younger minors (see, e.g., Joyce et al, 2006). For our control group in the D-DD analysis, we use rates for 18 year olds and, as an alternative, 18 and 19 year olds together.
County-level contraception data are from the Alan Guttmacher Institute (AGI) cliniclevel surveys that took place in 2001 and 2006. These provide data on the total number of
clients and the number of teenage clients for each county broken down by Title X-funded
clinics and other (non-Title X) clinics.3
A key issue which has affected many studies of parental consent for abortion is access
to services out-of-state. As Joyce et al (2006) point out, this problem is likely to be less acute
in the case of Texas due to the large geographical area which means accessing services outof-state is particularly difficult for many residents. We can imagine that the hassle cost of
independent travel to access services without parental assistance is likely to be particularly
high for minors. On the other hand, accessing out-of-state services is still likely to be an
issue for those residents living close to a state border. Further, cross-border travel will be
more important for county-level analysis such as we undertake below. To address this issue
in both our state- and county-level analyses, we consider the impact of excluding those
counties that directly border either another state or Mexico, i.e. those areas which are most
3
A potential further source of information on the behavioural response of teenagers in Texas to the
parental consent law would have been the Youth Risk Behavior Surveillance System (YRBSS). In principal,
YRBSS data on sexual behaviour are available biannually for 2001, 2003, 2005 etc. Unfortunately YRBSS data
for Texas is not available for the key year of 2003, whilst the data for 2001 used a radically different sampling
frame to that for subsequent surveys making comparisons over time difficult. See
www.dshs.state.tx.us/chs/yrbs/pages/yrbs_faq.shtm for details.
10
likely to be affected by travel to access services outside of the State. Further, for the countylevel analysis, we also control for the presence of clinics in bordering counties including
those counties within Texas and bordering countries in neighboring states.
5. Results
5.1 Impact on family planning attendance amongst minors
We first undertake some preliminary analysis to explore whether the available evidence is
consistent with the parental consent mandate having led to changes in family planning takeup. For this purpose, we use survey data of the number of female clients at publicly funded
family planning clinics collected by the Alan Guttmacher Institute (AGI). We compare the
rate of teenage clients reported at Texas clinics in 2001, before the funding change, and 2006,
after the funding change. No surveys were carried out in the intervening years.
Unfortunately data on take-up by adolescents are only available for under-20s and not
specifically for minors which is likely to make it more difficult for us to observe any effect of
parental consent.
Clearly changes in clinic attendance from 2001 to 2006 may be influenced by factors
other than parental consent. For this reason, we measure the change for adolescents relative
to the change for older women. We also measure the change for adolescents in Texas relative
to adolescents in other states in the Federal Region 6: Arkansas, Louisiana, New Mexico and
Oklahoma.
A useful feature of the AGI data is that the number of clients is provided separately
for Title X-supported clinics. As mentioned above, these clinics are federally funded and,
hence, were not directly affected by the 2003 parental support regulation. If any decrease in
total attendance at family planning clinics amongst adolescents is due to the parental consent
rule, we would expect the decrease to be dominated by non-Title X clinics. For this reason,
we measure the relative change in take-up for adolescents at Title X and non-Title X clinics.
The results of this exercise are reported in Table 1a. The deflators used for
calculating rates are the numbers of women in each age group reported by the AGI to be in
need of publicly supported contraceptive services.4 We also report p-values of a t-test of
differences between different groups.
4
The AGI classify women aged below 20 as being in need of publicly funded contraception if she is sexually
active, is fecund and neither intentionally pregnant nor trying to become pregnant. For women aged 20-44,
there is an additional requirement that her family income is below 250% of the federal poverty level (see
http://alanguttmacherinstitute.org/pubs/win/winmethods2006.pdf ).
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Between 2001 and 2006, the estimated rate of attendance by teens at publicly funded
family planning clinics in Texas went down from 36.9 to 25.2, a reduction of 31.7%. In other
Region 6 states, the rate of attendance actually increased by 2.6% giving a relative difference
of 34%. The rate of attendance for older women in Texas decreased by 15% and this
suggests that some of the decrease amongst adolescents may have been part of a broader
trend specific to Texas. However, the relative decrease for adolescents compared to older
women in Texas is still just under 16%. All these relative differences are strongly
statistically significant. We also calculate the difference-in-difference-in-differences by
comparing the relative change in Texas (i.e. adolescents to older women) to the relative
change in the other Region 6 states. In this case, the relative percentage decrease for Texas
adolescents is lower (5.9%) but still statistically significant at conventional levels.
A complementary approach is to estimate the relative change to attendance at affected
(non-Title X) and unaffected (Title X) clinics and we report these results in Table 1b.
Attendance by teenagers at affected clinics decreased by 36.9% and at unaffected clinics by
24.8%, a relative decrease of 12.2%. Amongst older women, attendance at affected clinics
decreased by 12.5% and at unaffected clinics by 19.4%. The implied difference-indifference-in-differences effect on teenagers at affected clinics is a decrease of 19.0%.
Again, all differences are statistically significant at conventional levels.
A further issue is whether clinic attendance between the two periods may have been
affected by other changes not linked to parental consent. The obvious examples are changes
to the number of clinics in each county between the periods and shifts in the numbers from
different ethnic/racial groups. For this reason, we estimate a regression model using counties
as the unit of observation. The model we estimate is:
attendanceit =  consent + X + uit
where attendance is the rate of attendance in each county (deflated by the total female
population in the relevant age group), i; t takes the values 2001 and 2006; consent is a
dummy variable for the year 2006 when the parental consent law was in effect; X is a vector
of other variables that may have affected clinic attendance, specifically the proportion of the
population that is Hispanic (Hispanic), the proportion that is black (Black) and the number of
family planning clinics per 1000 population (clinics).
We include fixed effects for each county and, due to the fact that some observations
of the dependent variable are zero, estimate the model in levels (rather than in logs) and
weight the regressions by the female population in each county. We estimate the model for
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teenagers and older women (using the population aged 15 to 19 and 20 to 44, respectively)
and also separately for those counties with at least one affected clinic and for those counties
with no affected clinics.
The coefficients on the various models are reported in Table 1c. The results are
consistent with the univariate analysis above. Looking at all counties and after controlling
for the number of clinics and racial/ethnic mix, the rate of family planning take-up is
estimated to go down by 6.3 after the imposition of parental consent for state-funded
contraception, representing a drop from the mean 2002 level of about 50%. When we split up
the sample, we find that the decrease is considerably larger for counties with at least one
affected clinic than those without (a decrease of 7.6 versus 2.14). The decrease for older
women is very much smaller and statistically insignificant. Further, for older women, we
observe very little difference in the parental consent effect between counties with an affected
clinic and those without.
So although the estimated effect varies depending on the comparison group and
methodology, there is consistent and strong evidence that attendance by adolescents at family
planning clinics decreased considerably before and after the change to parental consent in
2003. Further, the breakdown by those clinics affected and unaffected by the change is
consistent with the parental consent statute being the cause of a significant part of that
decrease. Given that the data on adolescents include older teenagers who would have been
unaffected by the parental consent law, it is likely that the magnitude of the impact on minors
was even greater than that suggested by the discussion above.
The numbers of adolescents who appear to have been affected by the parental consent
change are significant. On the assumption that the observed relative decreases in family
planning attendance can be attributed to those affected by the parental consent ruling (i.e.
minors), the estimated change relative to older women in Texas (the D-D estimate in Table 1a
of 15.9%) would imply more than 20,000 fewer minors attending family planning clinics
annually. Frost, Henshaw and Sonfield (2010) argue that, on average, 208 unintended
pregnancies are averted for each 1000 attendees at publicly funded clinics. Other things
equal, this implies that the parental consent ruling should have increased unintended
pregnancies amongst Texan minors by over 4,000 per year. Even on the basis of the smallest
estimated effect of 5.9% (the DDD estimate from Table 1b) this implies a potential 1,600
extra pregnancies.
Of course other things are not equal in that some of the affected minors will have
accessed alternative means of family planning such as purchasing contraception or crossing
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state or federal lines. Other minors may have chosen to reduce (or eliminate) their
engagement in risky sexual activity. Depending on the relative numbers in each of these
categories, the actual impact on unintended pregnancies is impossible to ascertain a priori.
We now go on to attempt to estimate the actual impact of mandating parental consent for
state-funded contraception on pregnancy, birth and abortion rates amongst minors.
5.2 Impact on pregnancy and abortion rates amongst minors
5.2.1 State–level estimates
Figure 1 illustrates the trend in pregnancy rates in Texas before and after the parental consent
ruling for three age groups: 18 year olds (the control group), under-18s (i.e. all those affected)
and under-16s. Differences in pregnancy rates across ethnic and racial boundaries have been
well documented. For this reason we present trends for the whole population in each age
group and for three racial and ethnic sub-groups: non-Hispanic whites, non-Hispanic blacks
and Hispanics. For ease of comparison, all rates are normalized to 100 in 2002.
The graphs provide little evidence that conception rates amongst minors increased
(either absolutely or relative to the rate amongst 18-year olds) from the introduction of
parental consent in 2003. Pregnancy rates for all groups are decreasing the years
immediately prior to the parental consent mandate being introduced. Rates continue to
decrease in 2003 (the first year in which the mandate was in effect), but the 18-year old rate
starts to increase from 2004. The rate for under-18s decreases relatively less fast in the first
year of the mandate but (relatively) faster in subsequent years. For under-16s, the rate
decreases faster than that for 18 year olds in each year after the mandate. The racial/ethnic
sub-groups show a similar pattern with the exception that the rate for under-18 blacks
decreases faster than that for 18 year olds even in 2003.
In Table 2a we report the differences (D) and relative differences (DD) for each age
group and racial/ethnic sub-group between 2002 (the year before the mandate) and 2003-5
(the first three years of the mandate). In all cases, the point estimates of the relative
differences are negative, but they are generally small in magnitude and statistically
insignificant. The point estimates of the relative differences tend to be somewhat larger for
younger teenagers and we find statistically significant, negative effects, for some of the
racial/ethnic sub-groups.
In Table 2b we report the relative differences (DDs) for a number of alternative
specifications. These can be summarized as follows:
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(i)
To help disentangle any difference between short and long and run effects, we report
separate estimates for each year from 2002 to 2005.
(ii)
We report effects on abortion and birth rates separately. Note that separate estimates
for abortion and birth rates are not reported here for reasons of space but are available
on request from the authors.
(iii)
We alter the definition of the control group in two ways. First, some of those who
conceive aged 18 are likely to have made decisions about contraceptive use when they
were still 17 and, hence, will have been affected by the parental consent mandate. To
allow for this, we exclude from the control group those aged younger than 18 and
three months. Second, we expand the control group to include also those aged 19 at
conception.
(iv)
A related issue is that some minors who conceived in 2003 will have accessed
contraceptive services during 2002, before the parental consent mandate was in place.
To allow for this, in the third column of Table 2b, we report estimates based on the
age of the mother at the likely time of any visit to a family planning clinic, namely
three months before conception.
(v)
We control for the possibility of cross-border travel in two ways. First, we exclude
from the analysis any county which borders either Mexico or another U.S. state.
Second we report the relative difference for rural counties alone. The latter
experiment reflects the fact that some urban areas in Texas cover more than one
county and that, in such cases, accessing clinics in neighboring counties is likely to be
much easier.
Consistent with the baseline estimates, the relative differences in these alternative
specifications are generally small, negative and, for under-18s, of low statistical significance.
The estimated effects tend to become more negative, the further away we get from the
introduction of the policy in 2003 and, in 2005, we observe a statistically significant
reduction in relative pregnancy rates for under-16s. This is consistent with the argument of
Arcidiacono et al (2011) that teenagers are more likely to change their behavior to avoid risk
in the long rather than short run. We also find significantly negative effects for under-16s in
some of the specifications, notably when 19-year olds are included in the control group, using
estimated age at clinic visit and when excluding border counties.
To summarize, the state-level estimates provide no evidence that parental consent for
federally-funded contraception led to an increase in pregnancy rates for minors relative to
older teenagers, unaffected by the ruling. Indeed in some specifications we find a statistically
15
significant relative decrease in pregnancy rates for younger teens and there is also some
evidence of a differential effect in the short and long run. It is possible, however, that those
significant effects which are observed in some of the state-level estimates are due to
nationwide effects that are contemporaneous with, but not caused by, the Texas parental
consent mandate. For this reason, we now go on to use the county-level data to investigate
whether those areas with clinics that were directly affected by the parental consent mandate
experienced significantly different changes in pregnancy rates to those areas without such
clinics.
5.2.2 County-level estimates
In Tables 3a and 3b, we report the county-level DD and DDD estimates of the effect of
parental consent for state-funded contraception on our two treatment groups: under-18s and
under-16s. In each case, we report separate estimates for 2003, 2004 and 2005, all relative to
the base year of 2002. Once we have dropped observations not within the common support
region of the propensity score estimator, the sample size is 236 counties for the under-18
estimates (comprising 110 counties in the treatment group and 126 in the control) and 233 for
the under-16 estimates (110 in the treatment and 123 in the control).
The sign of the estimated effects varies depending on the year and the treatment
group. For both age groups, the relative difference (DDD) is positive in the first year of
parental consent (2003) but negative in later years. However, none of the estimated effects
approach statistical significance at conventional levels.5
We next go on to report (in Tables 4a and 4b) regressions in which the treatment
effect can vary for different racial/ethnic groups. We find some evidence that the effects are
relatively different for Hispanics. For example, both the DDD estimates in 2003 suggest that
parental consent had a smaller effect for Hispanics than for whites. However, the overall
impact on pregnancy rates continues to be statistically insignificant in every case.
In Tables 5a and 5b we report the DD and DDD estimates for a series of robustness
checks and alternative specifications. These include the same checks that we carried out for
the state-level estimates along with three further checks as follows:
(i)
We specify pregnancy rates in natural logarithms rather than levels. This allows us to
interpret the coefficients as percentage changes, but does mean that counties with zero
observations in a particular category are dropped.
5
These (and subsequent results) are robust to the use of alternative sets of variables in the probit model
16
(ii)
We consider two alternative approaches to defining which counties are in the
treatment and/or control categories. The first alternative approach (Treatment
definition 2) is to exclude from the treatment group any county in which there is a
Title X clinic. The motivation for this is that in such counties, minors who would
have attended an affected (i.e. non-Title X clinic) will find it relatively easy to switch
to their (unaffected) local Title X clinic. The second alternative (Treatment definition
3) further controls for the possibility that affected minors will switch to an unaffected
clinic in a neighboring county, either within or outside the state. With this approach,
we exclude from the treatment group any county whose bordering counties have more
than one unaffected (i.e. Title X) clinic, whilst we exclude from the control group any
county whose bordering counties have more than one unaffected (i.e. non-Title X)
clinic. Although these approaches may allow a more precise measurement of the
effect of the parental consent mandate, they do lead to a considerable reduction in the
sample sizes, especially after imposing the common support condition. For Treatment
definition 2 the total sample sizes go down to 125 counties for the under-18 estimates
(72 in the treatment and 53 in the control) and 135 for under-16s (72 in the treatment
and 63 in the control). For Treatment definition 3, the sample sizes go down to just
47 for under-18s (25 in the treatment and 22 in the control) and 45 for under-16s (25
in the treatment and 20 in the control).
(iii)
To control for the possibility that counties with particularly small populations may be
overly weighted in the estimation, we exclude any county with a population in the
main childbearing years (between 15 and 44) of less than 500. This results in 9
counties being dropped from the analysis. In an alternative approach, we also
estimate the DD and DDD models using regressions weighted by the female
population aged 15 to 19 rather than by propensity scores.6
For under-18s (reported in Table 5a), the alternative specifications show a similar
pattern in the sign of effects to the state-level estimates in that the estimated effects are more
often negative (or less positive) in later years and for abortion rates and are more often
positive for birth rates. The magnitude of the coefficients varies considerably across the
specifications and in particular for alternative treatment definitions, but none of the estimated
differences are statistically significant at the 5% level.
6
The results are robust to alternative cut-off points for defining small counties. Note that it is not possible to
combine population weights with the propensity score weights in our main estimates.
17
The results for under-16s are reported in Table 5b. Again, the signs of the effects
follow a similar pattern to those from the state-level estimates, with a mixture of positive and
negative effects. However, in contrast to the state-level, none of the negative effects are
statistically significant. In the case of Treatment Definition 3 in 2005, the DD estimate is
positive and strongly significant. The small sample size in this specification, along with the
fact that the statistical significance of this estimate is not robust to the DDD estimation, limits
the inference that can be placed on this estimate. It does, however, stand as a notable
exception to the general pattern of results.7
To summarize, using both state-level and county-level data, we find very little
evidence that the introduction of mandatory parental consent for the provision of state-funded
contraception to minors in Texas in 2003 led to an increase in pregnancies amongst minors.
Our point estimates provide some evidence that parental consent may have had different
effects for younger relative to older minors, for abortion relative to birth rates and in the long
run relative to the short term. Rarely, however, do we find the estimated effects to be
statistically significant.
6. Discussion and Conclusions
Several legislatures in the U.S. and elsewhere continue to discuss the most appropriate way to
involve parents in minors’ decisions surrounding sexual health. Texas is one of just two
states in which parental consent has been made mandatory before state-funded contraception
can be provided to minors. Economic models of teenage behavior suggest that the impact of
parental consent for contraception will have ambiguous effects on pregnancy rates amongst
minors. To the extent to which parental consent restricts the take-up of contraception
amongst minors, pregnancy rates will increase. However, if some minors reduce the level of
sexual risk taking, pregnancy rates may decrease. Previous work, based on conjectural
responses of minors, predicted that net effect of the Texas parental consent mandate would be
to increase the unwanted pregnancy rate amongst minors rate by a very considerable amount.
This paper has provided the first test of these predictions using actual data before and after
parental consent was introduced in 2003, and using robust statistical methodology that
controls for both observable and unobservable characteristics affecting county-level Title X
clinic attendance.
7
This magnitude and significance of this estimate are also not robust to other specifications, e.g. estimating in
logs and excluding border counties.
18
At the state level, we find no evidence that mandating parental consent for statefunded contraception increased pregnancy rates amongst minors. For the youngest age group
(those aged under-16), there is some evidence that, at the State level, pregnancy rates went
down after the parental consent mandate relative to older teenagers who continued to be able
to obtain state-funded contraception without parental consent. We also use statistical
matching estimators on county-level data to compare the changes in pregnancy rates between
counties with family planning clinics affected by the mandate relative to those counties
without such clinics. This approach reveals very little impact from the parental consent
mandate, even for the under-16 group.
Taken together, the evidence suggests that, in contrast to the predictions of the
conjectural evidence, parental consent for state-funded birth control in Texas does not appear
to have increased underage pregnancy rates in the state. One explanation for this finding is
that minors (in aggregate) respond to actual parental involvement laws by reducing their level
of risky sexual activity to a greater extent than suggested by their conjectural responses to
potential laws. An alternative (and possibly complementary) explanation is that minors were
more successful than anticipated in accessing birth control from alternative sources that were
not subject to the parental consent statute. The fact that our findings are robust to controls for
cross-border travel suggests that such substitution is unlikely to explain our results fully.
However, the fact that we are not directly able to observe take-up of birth control by minors
from different sources, means that it cannot be discounted.
Our findings will be of most direct relevance to other states considering mandating
parental consent for the provision of state-funded birth control to minors. The evidence we
present here suggests that the risk of thereby increasing rates of underage pregnancy is low.
We can be less sure about whether our results would generalize to broader parental consent
mandates. The results may well have been different had parental consent been mandated for
the provision of birth control to minors from federally funded clinics too. That said, the
Texas statute provides the only large-scale change in parental consent legislation to have
been enacted in the world and, as such, the experience of the Texan law will be of
considerable interest to any legislature, in the U.S. or overseas, considering the issue of
parental involvement for birth control.
Finally, our results suggest that policy makers and academics should exercise caution
before drawing policy inferences from simulation work based on conjectured, rather than
actual, responses.
19
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21
Figure 1: Pregnancy rates in Texas by age, race and ethnicity, 2000-2006
1st year of
parental consent
110
120
110
2002=100
2002=100
105
100
100
90
95
90
80
2000
2002
2004
2006
2000
year
All 18s
All u16s
120
2002
2004
2006
year
All u18s
White 18s
White u16s
White u18s
110
1st year of
parental consent
1st year of
parental consent
105
2002=100
110
2002=100
1st year of
parental consent
100
100
95
90
90
80
85
2000
2002
2004
2006
year
Black 18s
Black u16s
2000
2002
2004
year
Black u18s
Hispanic 18s
Hispanic u16s
22
Hispanic u18s
2006
Table 1a: Relative impact of parental consent on family planning attendance rates amongst
teenagers
Texas
Rest of Region 6
U20
20-44
U20
20-44
2001
36.9
41.4
39.3
40.8
2006
25.2
34.8
40.4
46.0
% change
-31.7***
-15.9***
2.6***
12.6***
(0.24)
(0.15)
(0.37)
(0.24)
DD
-15.9***
-10.0***
(0.28)
(0.44)
DDD
-5.9***
(0.52)
Notes
(i) Region 6 is the Federal Region comprising Arkansas, Louisiana, New Mexico, Oklahoma and Texas.
(ii) Rates are calculated per 100 women classified by AGI as being in need of publicly supported contraceptive
services.
(iii) Standard errors for the difference in the percentage changes are in parentheses and are calculated using the
method described in www.census.gov/acs/www/Downloads/data_documentation/Accuracy/PercChg.pdf
(iv) Significant at 10%; ** significant at 5%; *** significant at 1%
Table 1b: Relative impact of parental consent on family planning attendance rates amongst
teenagers: affected and unaffected clinics
U20
20-44
Affected Unaffected Affected Unaffected
clinics
clinics
clinics
clinics
2001
21.2
15.8
21.3
20.0
2006
13.4
11.9
18.7
16.2
-24.8***
-12.5***
-19.4***
％ change -36.9***
(0.32)
(0.43)
(0.25)
(0.24)
(SE)
DD
-12.2***
6.9%***
(SE)
(0.54)
(0.34)
DDD
-19.0***
(SE)
(0.64)
Notes
(i) Unaffected clinics are family planning clinics receiving Title X funding.
(ii) Rates are calculated per 100 women classified by AGI as being in need of publicly supported contraceptive
services.
(iii) Standard errors for the difference in the percentage changes are in parentheses and are calculated using the
method described in www.census.gov/acs/www/Downloads/data_documentation/Accuracy/PercChg.pdf
(iv) Significant at 10%; ** significant at 5%; *** significant at 1%
23
Table 1c: County-level regression estimates of impact of parental consent on family planning
attendance
U20
20-44
All
Affected Non-affected
All
Affected
Non-affected
counties
counties
counties
counties
consent
-6.27*** -7.63*** -2.14*
-1.31
-1.26
-1.08
(2.18)
(27.93)
(1.10)
(1.47)
(1.97)
(0.93)
clinics
1.38
0.12
2.76**
12.90*** 12.85*
12.90**
(0.87)
(12.86)
(1.15)
(4.24)
(6.50)
(5.37)
Hispanic
0.22
0.55
-0.36
0.023
0.028
-0.06
(0.18)
(0.74)
(0.59)
(0.08)
(0.94)
(0.06)
Black
0.23
0.22
0.77
0.06
0.065
0.13
(0.71)
(1.01)
(0.65)
(0.18)
(0.31)
(0.14)
Sample size
483
County effects yes
198
yes
285
yes
482
yes
Notes
(i) Regressions are weighted by female population in each county.
(ii) Standard errors in parentheses.
(iii) Significant at 10%; ** significant at 5%; *** significant at 1%.
24
197
yes
285
yes
Table 2a: State-level estimates of effect of parental consent on pregnancy to minors
Variable
Age group Pregnancy
Pregnancy
D
DD
rate 2002
rate 2003-5
18
132.79
127.6
-4.61***
n/a
( 8.45)
U18
69.39
66.4
-4.72***
-0.12
All
(6.50 )
(1.07)
U16
17.67
16.49
-7.02***
-2.41
( 1.25)
(1.51)
18
87.13
82.45
-6.02***
n/a
(1.52 )
Non-Hispanic U18
36.55
34.42
-6.21***
-1.84
White
(1.32 )
(2.01)
U16
7.58
6.63
-13.52***
-7.49***
( 2.90)
(3.27)
18
156.49
153.2
-2.48
n/a
(2.19)
Non-Hispanic U18
81.06
75.14
-8.24***
-5.75**
Black
(1.67)
(2.76)
U16
22.59
20.67
-9.09***
-6.61*
(3.04)
(3.75)
18
183.50
176.3
-4.85***
n/a
(1.19)
U18
107.90
102.0
-6.27***
-1.42
Hispanic
(0.86)
(1.47)
U16
28.53
26.22
-8.69***
-3.84*
(1.59)
(1.98)
Notes:
(i) Rates are per 1000 women at estimated age of conception. For under-18s, the female population aged 15-17
is used as the deflator, whilst for under-16s, the female population aged 13-15 is used.
(ii) D is the difference in (log) rates for the respective age group from 2002 to 2003-5; DD is the difference
relative to 18 year olds, as specified in equation (1). Coefficients are multiplied by 100 so that they can be
interpreted as percentage (relative) differences
(iii) Standard errors in parentheses.
(iv) Significant at 10%; ** significant at 5%; *** significant at 1%.
.
25
Table 2b: State-level DD estimates of effect of parental consent: alternative specifications
Specification
Under 18
Under 16
Baseline (from Table 2a)
-0.12
-2.41
(1.07)
(1.51)
2002 vs 2003
1.58
-0.23
(1.31)
(1.86)
2002 vs 2004
-0.30
-2.25
(1.30)
(1.86)
2002 vs 2005
-2.19*
-4.71**
(1.30)
(1.85)
Abortion rates
3.85
-3.19
(2.47)
(3.64)
Birth rates
-1.53
-2.99*
(1.16)
(1.65)
Control group: 18.25 < 19 -0.71
-3.01*
(1.15)
(1.57)
Control group: 18.25 – 19 -1.18
-3.47**
(0.89)
(1.39)
Est. age at clinic visit
-1.42
-4.32**
(1.03)
(1.44)
Excluding border counties -1.91
-3.66**
(1.19)
(1.69)
Excluding urban counties 1.08
0.67
(2.73)
(3.89)
Notes:
(i) Estimates are the (log) differences from 2002 relative to the differences in the control group (18-year olds
unless stated otherwise) as specified in equation (1). Coefficients are multiplied by 100 so that they can be
interpreted as percentage (relative) differences.
(ii) Standard errors in parentheses.
(iii) Significant at 10%; ** significant at 5%; *** significant at 1%.
26
Table 3a: Treatment effects on under-18 pregnancy rates 2003, 2004 and 2005 versus 2002:
DD and DDD combined with propensity score reweighed regressions
DD
treatment
poverty
lag pregnancies
urban
border
Hispanic
Black
Title X (2001)
constant
Sample size
Adjusted R2
2003
1.387
(2.627)
21.815
(42.511)
-0.424***
(0.079)
-2.547
(2.695)
3.360
(3.083)
0.009
(0.083)
-0.317
(0.196)
-3.441
(2.257)
-1.185
(5.232)
236
0.282
2004
-5.809
(4.417)
-104.880
(132.000)
-0.700***
(0.145)
-7.829
(7.085)
-4.073
(5.506)
0.538
(0.380)
0.609
(0.388)
-5.755
(3.968)
0.137
(14.185)
236
0.275
DDD
2005
-1.038
(3.406)
-78.937
(67.677)
-0.565***
(0.127)
-6.018
(4.506)
-7.675*
(4.011)
0.387**
(0.195)
0.256
(0.266)
-4.744
(2.963)
0.498
(7.939)
236
0.291
Notes:
(i) Standard errors in parentheses
(ii) Significant at 10%; ** significant at 5%; *** significant at 1%
27
2003
4.103
(10.907)
-72.365
(256.719)
-0.482
(0.351)
0.122
(14.373)
-1.745
(14.051)
0.715
(0.720)
-0.194
(0.871)
1.608
(11.489)
-6.519
(28.163)
236
0.036
2004
-10.434
(11.145)
-386.273
(358.593)
-0.661***
(0.163)
-23.878
(18.924)
-7.761
(13.814)
1.336
(1.035)
1.626
(1.062)
-11.743
(10.919)
29.537
(37.723)
236
0.084
2005
-7.261
(10.172)
-171.860
(203.342)
-0.629**
(0.288)
-11.674
(11.377)
-6.824
(13.268)
0.997*
(0.557)
0.755
(0.705)
-8.450
(7.773)
1.402
(23.791)
236
0.074
Table 3b: Treatment effects on under-16 pregnancy rates 2003, 2004 and 2005 versus 2002:
DD and DDD combined with propensity score reweighed regressions
DD
treatment
poverty
lag pregnancies
urban
border
Hispanic
Black
Title X (2001)
constant
Sample size
Adjusted R2
2003
0.026
(1.307)
-2.871
(15.858)
-0.559***
(0.097)
-2.257*
(1.261)
-1.252
(1.595)
0.007
(0.040)
-0.044
(0.079)
-1.557
(1.786)
1.500
(2.444)
233
0.379
2004
0.266
(1.314)
0.291
(16.780)
-0.582***
(0.094)
-2.047*
(1.176)
-1.714
(2.021)
-0.001
(0.041)
0.053
(0.076)
-3.140***
(1.159)
0.325
(2.711)
233
0.318
DDD
2005
-0.837
(1.995)
-86.904*
(52.312)
-0.563***
(0.088)
-5.445*
(2.969)
-2.822
(2.397)
0.280*
(0.155)
0.260
(0.163)
-3.053
(1.893)
6.585
(5.478)
233
0.270
Notes:
(i) Standard errors in parentheses
(ii) Significant at 10%; ** significant at 5%; *** significant at 1%
28
2003
2004
0.660
-5.746
(10.486)
(9.330)
-85.138
-264.558
(250.136) (239.040)
-1.420**
-0.690**
(0.583)
(0.320)
0.723
-17.908
(14.624) (13.520)
-7.315
-8.345
(13.198) (11.681)
0.832
0.886
(0.757)
(0.718)
0.319
1.076
(0.800)
(0.753)
-6.228
-13.537
(10.636)
(9.302)
-9.216
26.373
(27.270) (26.188)
233
233
0.063
0.042
2005
-4.733
(9.590)
-217.502
(192.065)
-0.482
(0.593)
-10.672
(10.967)
2.703
(11.971)
0.883
(0.541)
0.810
(0.661)
-8.725
(8.706)
10.905
(21.479)
233
0.024
Table 4a: Treatment effects on under-18 pregnancy rates 2003, 2004 and 2005 versus 2002:
DD and DDD combined with propensity score reweighed regressions by race/ethnicity
DD
DDD
Poverty
2003
2.191
(2.625)
-0.258**
(0.114)
-0.472
(0.294)
27.165
2004
-5.024
(4.305)
-0.334*
(0.199)
-0.155
(0.376)
-99.633
2005
-0.444
(3.240)
-0.269*
(0.155)
-0.058
(0.345)
-74.955
2003
8.005
(10.943)
-1.387***
(0.504)
-1.787
(1.134)
-46.354
2004
-9.832
(10.953)
-0.423
(0.569)
0.494
(0.985)
-382.193
2005
-5.708
(10.027)
-0.837
(0.570)
0.341
(1.120)
-161.415
lag pregnancies
(41.601)
-0.423***
(129.292)
-0.708***
(65.779)
-0.573***
(249.201)
-0.492
(354.225)
-0.685***
(198.208)
-0.664**
(0.079)
-2.211
(2.728)
4.345
(3.166)
0.082
(0.087)
-0.204
(0.223)
-3.385*
(1.989)
-6.018
(5.390)
236
0.294
(0.150)
-6.995
(6.561)
-3.176
(5.575)
0.647
(0.428)
0.607*
(0.328)
-5.416
(3.790)
-5.309
(12.680)
236
0.281
(0.125)
-5.287
(4.344)
-7.008*
(4.199)
0.477**
(0.220)
0.233
(0.278)
-4.431
(3.012)
-3.772
(8.157)
236
0.299
(0.356)
2.585
(13.736)
2.932
(15.093)
1.131
(0.795)
0.171
(0.824)
2.347
(12.158)
-31.182
(27.834)
236
0.067
(0.166)
-22.218
(17.619)
-7.202
(14.425)
1.496
(1.179)
1.400
(0.885)
-10.910
(10.641)
23.891
(34.934)
236
0.084
(0.293)
-8.944
(10.924)
-5.184
(14.295)
1.293**
(0.638)
0.514
(0.670)
-7.173
(7.714)
-10.931
(26.597)
236
0.094
Treatment
treatment*Hispanic
treatment* Black
Urban
Border
Hispanic
Black
Title X (2001)
constant
Sample size
Adjusted R2
Notes:
(i) Standard errors in parentheses
(ii) Significant at 10%; ** significant at 5%; *** significant at 1%
29
Table 4b: Treatment effects on under-16 pregnancy rates 2003, 2004 and 2005 versus 2002:
DD and DDD combined with propensity score reweighed regressions by race/ethnicity
DD
treatment
treatment*Hispanic
treatment* Black
poverty
lag pregnancies
urban
border
Hispanic
Black
Title X (2001)
Constant
Sample size
Adjusted R2
DDD
2003
2004
2005
2003
0.053
(1.324)
-0.032
(0.059)
0.007
(0.201)
-2.251
(15.737)
-0.565***
(0.100)
-2.153*
(1.259)
-1.207
(1.613)
0.019
(0.041)
-0.049
(0.088)
-1.554
(1.768)
0.959
(2.386)
233
0.374
0.262
(1.336)
0.073
(0.057)
-0.081
(0.123)
-0.841
(15.725)
-0.563***
(0.098)
-2.343*
(1.202)
-1.743
(2.024)
-0.032
(0.048)
0.085
(0.088)
-3.166***
(1.166)
1.450
(2.893)
233
0.319
-0.438
(1.985)
-0.159
(0.118)
-0.259
(0.168)
-82.601
(51.420)
-0.575***
(0.101)
-5.212*
(2.786)
-2.277
(2.616)
0.330*
(0.186)
0.319**
(0.159)
-3.131
(1.897)
3.441
(5.290)
233
0.277
3.254
(10.646)
-1.527***
(0.551)
-1.108
(1.118)
-49.640
(238.161)
-1.627***
(0.615)
4.268
(13.395)
-3.613
(14.245)
1.371
(0.875)
0.477
(0.712)
-6.548
(11.254)
-37.204
(25.937)
233
0.108
Notes:
(i) Standard errors in parentheses
(ii) Significant at 10%; ** significant at 5%; *** significant at 1%
30
2004
-6.311
(9.503)
-0.186
(0.539)
0.847
(1.023)
-264.371
(234.248)
-0.781**
(0.351)
-16.551
(12.408)
-8.977
(12.115)
0.995
(0.867)
0.806
(0.621)
-13.274
(9.208)
24.531
(24.750)
233
0.041
2005
-4.197
(9.812)
-0.766
(0.546)
0.297
(1.114)
-203.280
(189.473)
-0.643
(0.620)
-8.090
(10.372)
3.621
(12.962)
1.190*
(0.641)
0.638
(0.644)
-8.622
(8.342)
-1.781
(24.043)
233
0.041
Table 5a: Treatment effects for under-18s: alternative specifications
Specification
DD
2003
Baseline (from Table 3a)
Log (pregnancies)
Abortion rates
Birth rates
Treatment definition 2
Treatment definition 3
2004
1.387
-5.809
(2.627) (4.417)
0.024
-0.024
(0.050) (0.049)
-0.598
0.370
(1.271) (1.542)
1.985
-6.179
(2.513) (4.103)
-0.343 -14.259
(3.906) (9.299)
-13.140* 3.813
(7.345) (10.847)
2003
2004
2005
-1.038
(3.406)
0.054
(0.047)
0.300
(2.264)
-1.338
(2.858)
-2.584
(6.395)
11.470
(7.550)
4.103
(10.907)
0.044
(0.084)
5.398
(3.416)
-1.295
(10.144)
2.061
(21.119)
13.372
(22.543)
1.567
(9.899)
-3.677
(7.829)
5.826
(9.469)
1.866
(13.053)
6.962
(8.924)
4.616
(14.025)
3.752
(4.435)
-10.434
(11.145)
-0.020
(0.065)
3.295
(2.981)
-13.729
(11.163)
-36.137
(23.218)
7.987
(19.697)
-12.411
(10.681)
-11.810
(10.579)
-12.144
(8.571)
-12.219
(15.246)
-1.550
(6.277)
-15.418
(13.774)
2.157
(3.895)
-7.261
(10.172)
0.012
(0.084)
2.025
(2.971)
-9.286
(8.946)
-17.663
(17.361)
24.747
(26.934)
-11.459
(9.795)
-7.770
(5.978)
5.631
(11.797)
-4.339
(11.271)
-3.967
(9.358)
-13.266
(12.884)
7.938*
(4.721)
Control group: 18.25 < 19 n/a
n/a
n/a
Control group: 18.25 – 19
n/a
n/a
n/a
Est. age at clinic visit
-1.161
(2.714)
1.506
(3.336)
0.770
(2.598)
3.154
(3.272)
-0.013
(1.408)
-6.882
(5.000)
-5.486
(5.920)
-3.195
(2.867)
-6.868
(5.554)
-0.512
(1.565)
2.906
(3.793)
-0.730
(3.917)
0.568
(3.050)
0.262
(4.364)
0.176
(1.678)
Excluding border counties
Excluding small counties
Excluding urban counties
Population weighted
DDD
2005
Notes:
(i) In each case, the coefficient on treatment is reported along with standard errors in parentheses.
(ii) significant at 10%; ** significant at 5%; *** significant at 1%.
31
Table 5b: Treatment effects for under-16s: alternative specifications
Specification
DD
2003
2004
2005
2003
Baseline (from Table 3a)
0.026
0.266
-0.837
0.660
(1.307)
(1.314)
(1.995)
(10.486)
Log (pregnancies)
-0.043
-0.108
-0.087
-0.052
(0.083)
(0.070)
(0.079)
(0.104)
Abortion rates
0.061
-0.032
-1.155
4.230
(0.812)
(0.847)
(1.603)
(2.961)
Birth rates
-0.035
0.297
0.318
-3.569
(1.166)
(1.517)
(1.486)
(9.966)
Treatment definition 2
0.018
0.594
-2.491
-7.317
(1.690)
(2.010)
(3.941) (21.017)
*
Treatment definition 3
0.321
7.454
9.307***
9.291
(3.298)
(4.160)
(3.104) (20.834)
n/a
n/a
Control group: 18.25 < 19 n/a
1.070
(9.822)
n/a
n/a
Control group: 18.25 – 19 n/a
-4.109
(8.381)
Est. age at clinic visit
2.126
2.189
0.169
5.271
(1.736)
(1.513)
(2.075)
(9.813)
Excluding border counties -0.308
0.817
-0.854
0.367
(1.424)
(1.468)
(2.081)
(11.197)
Excluding small counties
-0.007
0.560
0.385
5.388
(1.277)
(1.261)
(1.426)
(7.900)
Excluding urban counties
0.836
0.511
-0.657
-1.005
(1.628)
(1.704)
(2.530) (13.820)
Population weighted
-0.818
-0.281
-0.796
2.811
(0.807)
(0.773)
(0.804)
(4.279)
DDD
2004
-5.746
(9.330)
-0.126
(0.089)
2.793
(2.524)
-8.539
(9.322)
-23.762
(18.898)
10.509
(20.449)
-7.484
(8.724)
-3.272
(8.955)
-6.511
(9.059)
-1.545
(10.203)
0.707
(6.510)
-11.059
(11.957)
2.351
(3.681)
Notes:
(i) In each case, the coefficient on treatment is reported along with standard errors in parentheses.
(ii) significant at 10%; ** significant at 5%; *** significant at 1%.
32
2005
-4.733
(9.590)
-0.100
(0.106)
1.122
(2.737)
-5.855
(8.457)
-17.173
(15.924)
14.505
(23.372)
-8.818
(8.842)
-4.565
(5.756)
1.889
(11.957)
-6.164
(9.988)
-1.226
(8.451)
-10.934
(12.559)
6.892
(4.382)
Appendix
Table A1: Definition and Source of Variables
Variable
Description
Conceptions ending in either a live birth or an abortion per
pregnancy rate
treatment
poverty
thousand population. Miscarriages are excluded miscarriages.
Population is the female population for the relevant area, age group
and race/ethnicity classification. For under-16 rates, the female
population aged 13-15 is used.
Pregnancy rate lagged by two years.
Conceptions per thousand population resulting in an induced
abortion by area of residence.
Conceptions per thousand population resulting in a live birth by
area of residence.
= 1 for years in which the parental consent ruling was in force
(from 2003 on); = 0 otherwise.
=1 if consent = 1 for affected counties only; = 0 otherwise.
Total percentage of persons living below the poverty level
urban
=1 if the county is in an urban area; = 0 otherwise
border
=1 if the county borders either Mexico or another U.S. state; = 0
otherwise
attendance
Number of female contraceptive clients served at publicly
supported family planning clinics.
clinics
Total number of publicly funded family planning clinics.
Title X
Number family planning clinics supported by the federal Title X
program.
Lag pregnancies
abortion rate
birth rate
consent
33
Source
Texas DSHS Center for
Health Statistics: supplied to
the authors
Texas DSHS as above
Texas DSHS as above
n/a
n/a
Texas DSHS Center for
Health Statistics, Texas
Health Facts Profiles
(various years).
Texas DSHS Center for
Health Statistics, County
Designations.
Texas DSHS Center for
Health Statistics, County
Designations.
Guttmacher Institute,
Contraceptive Needs and
Services (2001 and 2006)
Contraceptive Needs and
Services (as above)
Contraceptive Needs and
Services (as above)
Table A1: Marginal effects from the Probit regression of the determinants of county-level
Title X clinic attendance
(1)
(2)
U18s
U16s
Poverty
2.048**
1.945**
(0.876)
(0.879)
Lag pregnancies -0.002
-0.006**
(0.001)
(0.003)
Urban
0.299***
0.288***
(0.089)
(0.090)
Border
0.136
0.138
(0.089)
(0.090)
Hispanic
0.007***
0.008***
(0.002)
(0.002)
Black
0.008*
0.008*
(0.005)
(0.005)
Title X (2001)
-0.233***
-0.248***
(0.061)
(0.062)
Sample size
254
254
Notes:
(i) Standard errors in parentheses
(ii) Significant at 10%; ** significant at 5%; *** significant at 1%
34