Abortion Policy And Fertility In The 1990s
Work on abortion and health in 1990s was shaped by the advances in applied microeconometrics. A series of seminal papers in the econometric literature described the conditions that must hold before instrumental variable methods would yield even limited estimates of treatment effects. The 1990s also saw more emphasis on transparent sources of variation and the quality of the comparison group. The difference-indifference (DD) methodology became popular because it focused on the reduced form and plausible counterfactuals. There was also much more use of panel data given the attention to pre–post contrasts. Another development was interest in the effect of abortion policy on fertility. This relationship is key to the household production model. If researchers can not demonstrate a relationship between the price of fertility control and the number or timing of births, then abortion may not play an important role in the quality–quantity trade-off envisioned by its early proponents.
The most important policy change in the US was the legalization of abortion. This occurred largely in two steps. From September of 1969 through December of 1970, abortion became de facto or de jure legal in 5 states (Alaska, California, Hawaii, New York, and Washington) and the District of Columbia (Lader, 1974). Abortion became legal nationally with the US Supreme Court decision in Roe versus Wade in January of 1973. The two-step process toward national legalization provided plausibly exogenous sources of variation with which to identify the effect of the availability of abortion services on fertility. An early paper looked at the impact of the legalization of abortion in New York on teen birth rates in New York City in the years before Roe. Lacking data from a control state, the authors used an interrupted time series analysis to estimate the monthly change in White and non-White teen births after abortion became legal in July of 1973. They found that White and non-White births fell 14% and 18%, respectively, in the 24 months after the law went into effect.
Levine et al. (1999), however, were the first to exploit the staggered process of legalization within a DD strategy to obtain the most credible estimates of the effect of a decrease in the price of fertility control on birth rates. Using natality data from all 50 states and the District of Columbia, they contrasted changes in fertility from 1961 to 1980 among the early versus the later legalizing states. Overall birth rates fell almost 5% more among women in the early compared with later legalizing states. However, when the authors took account of distance to the nearest legalizing states, the results showed that birth rates fell 10% among those that lived more than 750 miles away from the nearest state in which abortion was legal. Surprisingly, there was no distance gradient for those who lived within 750 miles. Specifically, birth rates fell 4.5% regardless of whether women resided 250 miles away or between 250 and 750 miles from a state with legalized abortion. The study was a classic example of a DD and provided convincing evidence that the early legalization of abortion had an immediate effect on fertility. Some of these same authors would further exploit this natural experiment to analyze changes in well-being associated with changes in fertility.
Although induced abortion was declared a fundamental right, it remained highly controversial. State governments moved quickly to find the legal limits of regulation. Three state policies have dominated both the political discourse and academic research. The first is the Hyde Amendment, which prohibited the use of federal funds to cover the cost of an abortion unless the mother’s life is in danger. The second is PI laws which require that a physician notify or obtain consent from a parent or parents before performing an abortion on a minor, usually defined as girls less than 18 years of age. The third policy is a mandatory delay and counseling statute. This requires that women receive state-mandated information regarding the abortion procedure, the status of the fetus, and alternatives to abortion usually 24 h before the termination. Each policy has been used by economists to analyze changes primarily in abortion and birth rates, although some have looked at the reduced-form association with health. In this summary the focus is on a selected group of studies based on the quality of the design and their impact on subsequent work.
In 1976, Congress passed the Hyde Amendment, which bans federal funding of abortion in all but the most extreme circumstances. The statute prohibits expenditure of federal funds for abortion services except in cases where the continuation of the pregnancy threatened the woman’s life. Currently, 17 states use their own funds to pay for all or most medically necessary abortions sought by Medicaid recipients.
The impact of Medicaid financing restrictions has been analyzed extensively. A review by researchers at the Guttmacher Institute in 2009 listed 37 studies related to the Hyde Amendment. In this article, the focus is on studies by economists that use panel data designs or that exploit a particularly unique experiment. The Journal of Health Economics published two studies of the Hyde Amendment in the same issue in the Winter of 1996. In both the studies, researchers used a panel of states. In one study, authors analyzed abortion rates from 1974 to 1988, whereas in the other researchers used data from 1977 to 1988. Both studies found that the restrictions were associated with a decline in abortion rates of between 3% and 5%. One group of researchers used TSLS to account for the endogeneity of abortion providers; however, the instruments were not convincing. The authors used the natural logarithm of the number of hospitals to predict the natural logarithm of abortion providers and yet many hospitals provided abortions, which undermined the exclusion restriction. The other group of researchers analyzed birth and pregnancy rates in addition to abortion rates. They found that increases in the cost of an abortion lowered birth rates in models that used a 1-year lag in the Medicaid restrictions. Moreover, the decline in births was greater than the fall in abortion rates. The latter finding is hard to reconcile for as it suggests that the decline in births not only offsets the likely rise among some women who carry to term but also induces an even larger group to avoid pregnancy altogether.
Arguably the best ‘natural experiment’ of the Medicaid financing of abortions occurred in North Carolina (Cook et al., 1999). The State allocated a fixed sum of funds to be used by poor women for abortions as a substitute for resources restricted by the Hyde Amendment. However, between 1978 and 1994, the fund expired five times before the end of the fiscal year in June. The cutoff occurred once in months of December, January, and March and twice in the month of February. The authors found that the cutoff was associated with a fall in abortions and a commensurate rise in births. The effects were greater for Blacks than for Whites and for women with less than 12 years of schooling compared with those with more. Specifically, abortion among Blacks fell 9.5% overall, whereas births rose by 4.7%. In absolute terms, there was a one-to-one correspondence between the fall in abortions and rise in births among Blacks.
The study from North Carolina is particularly convincing. The timing of the funding cutoff varied by year and month and thus would have been difficult for a woman to anticipate. The authors found no jump in abortions in July as the fund was replenished. The fall in abortions coincided with a rise in births, and effects were greater among groups with higher rates of poverty. The study in North Carolina provides a useful contrast to the previous studies of publicly funded abortions in the US. There is an important trade-off between internal and external validity in these studies, which will be relevant in the discussions that follow. The study in North Carolina has the stronger internal validity, but it pertains to a single state. Nevertheless, the funding cutoff occurred five times, which strengthened the design considerably. However, the panel data studies have the advantage of analyzing changes in 50 states with more than 34 ‘natural experiments.’ However, the number of experiments is misleading. There is limited state variation in the timing of Medicaid funding restraints as the vast majority of restrictions went into effect in 1977 or 1981. Finally, the natural experiment in North Carolina was only able to address short-term changes in abortion and births, whereas the panel studies were able to test for longer term impacts, which may dissipate over time as women adjust to the restrictive funding environment. Despite these caveats, a clear conclusion is that the cutoff of public funding for abortions reduced abortion rates among poor women. The first-order effect should be a rise in births, for which the study in North Carolina provides convincing evidence.
Parental Involvement Laws
The Supreme Court’s decisions in Planned Parenthood of Central Missouri versus Danforth in 1976 and Bellotti versus Baird in 1979 made it constitutional for states to require minors seeking abortions to obtain parental consent or to notify their parents provided that there is an alternative approval mechanism such as a court bypass procedure. Thirtyeight states currently require parental consent or notification of at least one parent or in some instances other adults such as a grandparent or guardians.
Evaluation of PI laws on abortion and births has been hampered by limited data. Ideally, researchers would like agespecific abortion rates by state of residence from 1974 to 2008. These data do not exist. The CDC collects abortions by age for approximately 40 states, but they refer to abortions by state of occurrence. The Guttmacher Institute has used the CDC data to estimate abortions by state of residence, but the Guttmacher researchers acknowledge that their estimates do not take into account travel by subgroups. This becomes a major source of bias in studies of PI laws because resident minors leave the state in response to a PI requirement and nonresident minors stop coming into the state. Abortions by state occurrence will show a substantial drop in abortions to minors when in fact many abortions to minors that would have occurred in the state before the law are performed in other states after the law. This has been demonstrated repeatedly (Cartoff and Klerman, 1986). A second important issue is that researchers have used abortions and birth rates of 18and 19-year olds as either a counterfactual for changes in birth and abortion rates for minors or as a falsification test. However, the most affected group of minors is 17-year olds. They have the most pregnancies and they are the least willing to involve their parents. Yet, three-quarters of minors who are 17 years of age when they become pregnant will give birth as 18-year olds. As a result, a comparison group of 18-year olds in a DD analysis is contaminated because it includes a large proportion of girls who were exposed to the PI law during pregnancy when they were 17 years of age. Similarly, a falsification test in which the birth rates of 18or 19-year olds is regressed on a PI law may show little change or even a rise in births. Here too the test is compromised because the 17-year olds who were exposed to the law as minors gave birth when they were 18 years of age.
As with Medicaid financing restrictions, economists have tended to use panel data of state abortion rates to evaluate PI laws. One author reported that PI laws were associated with a 20% fall in the abortion rate of teens of 15–19 years of age. The major limitations were that the author used CDC occurrence data from 1978 to 1990, which fails to account for travel by resident and nonresident minors and the author included 18and 19-year olds who were unaffected by the law. Another economist used Guttmacher data on teen abortion rates by state of residence for 1985, 1988, 1992, and 1996. He reported a 15% decline in the abortion rate of minors. However, his data do not take into account movement across borders and he only had 4 years of nonconsecutive data. Two economists analyzed data from three states: South Carolina, Tennessee, and Virginia. They found little association with the conditional probability of abortion given pregnancy. They attributed the null finding to travel by minors out-of-state. However, pregnancy resolution as an outcome was uninformative about possible decreases in pregnancy in response to the law. Two other economists analyzed county birth rates from 1973 to 1988. They found that PI laws were associated with a 3% decrease in the birth rate of minors but a 2% decrease in the birth rate of teens of age 18 and 19 years. In absolute terms, however, the fall in the older teen birth rate exceeded that of minors, a result that could be interpreted as a relative rise in the birth rate of minors.
Finally, a study in Texas was able to overcome a number of the empirical challenges that have hampered previous studies (Joyce et al., 2006). First, the authors had data on abortions to residents of Texas. Second, they were able to collect data from the neighboring states as to the number of Texas minors that went out of state after the law. Few minors left Texas because all of the border states except New Mexico enforced a PI law. Third, the authors measured abortions and births by age at conception, which minimized the misclassification bias in previous work. They found that the Texas notification law was associated with a 16% fall in abortion rates among minors who were 17 years and 6–9 months of age at conception and a 4% rise in births. Subsequent work demonstrated that some minors who were almost 18 yeas of age when they conceived waited until they were 18 years of age to abort, even if the delay caused them to terminate substantially later in pregnancy. Finally, they showed that using age at the time of the abortion or birth and ignoring the misclassification resulted in a much larger fall in abortions with no rise in births. This provides some explanation for the findings by other economists who reported no change in births associated with PI laws. In all the other studies authors used age-specific birth rates based on the teen’s age at the time of birth and not at conception.
The studies of Texas by Joyce and colleagues are to the PI literature what the study by Cook et al. (1999) is to the literature on Medicaid financed abortions. Both studies have strong internal validity, given the design and quality of data, but both pertain to a single state, which limits their external validity. Studies that use state panels with many law changes would seem superior, but less accurate data on residents and the difficulty of accounting for trends in the outcomes have undermined their internal validity. This trade-off between internal and external validity continues in the studies of mandatory delay and counseling laws as will be shown next.
Mandatory Delay And Counseling
Many states require a waiting period between the time a woman has been counseled about her abortion and the actual procedure. About 23 states require a mandatory waiting period of 24 h. Utah requires a waiting period of 72, another state 18 h, and one state requires that counseling take place on a day before the abortion but did not specify the length of the waiting period. Four other states had mandatory counseling and waiting period laws whose enforcement had been enjoined. These laws specify that certain information must be given or offered to the women at the initial visit. The required counseling usually includes, among other things, the gestational age of the fetus, information about fetal development, the risks of abortion and childbirth, and resources available for pregnant low-income women. Some mandatory counseling and waiting period laws stipulate or have been interpreted to mean that a woman can be counseled via mail or phone about her procedure; others require that the woman be counseled in person, which usually means she must visit the facility twice – once for counseling and again for the procedure.
The constitutionality of mandatory delay statutes was not confirmed until the 1992 US Supreme Court decision Planned Parenthood of Pennsylvania versus Casey. Thus, there have been relatively few studies and few have found any significant impact of these policies on abortion and birth rates. One problem has been the use of state panels through 1997 or 1998. These studies were statistically underpowered as only a small percentage of women in these panels were exposed to the law. Another reason why these laws have had relatively little impact is because most states allow information to be given over the phone or the internet. This imposes relatively little burden on either the patient or the clinic and would only affect abortions if the required information was persuasive. A recent case-study analysis in Texas found no change in the abortion rate of Texas residents after the state required a 24 h delay and mandated information in January of 2004. The law did not have an inperson requirement as women could obtain the information over the internet (Colman and Joyce, 2011). In contrast, states that require that patients receive the mandated information in person, at least 24 h before the procedure, have demonstrated a greater impact on abortion rates. The burden of an inperson statute is potentially substantial if it necessitates that a woman who lives far from the clinic stay overnight. Mississippi provides such a case. The state imposed a mandatory delay and counseling law with an inperson requirement in August of 1992. Three studies of the law’s impact, all using different counterfactuals, found that the law was associated with approximately a 10% decrease in abortion rates, an increase in second trimester abortion rates, and a substantial rise in women leaving the state for an abortion. The key to each study was the quality of the data. Researchers were able to measure abortions to residents of Mississippi obtained in other states. They also had data on the gestational age of the fetus at the time of the termination. However, as with Medicaid financing of abortions and PI laws, the external validity of studies based on a single state is a key limitation.
What conclusion can bedrawn from analyses of state policies in the post-Roe era? The first is that raising the cost of abortion affects behavior. Abortion rates fall, women travel to less restrictive states, and abortions occur later in pregnancy. What is less clear is the magnitude of these changes. The impact of a policy depends on the availability of alternatives. Very poor women may be unable to raise the necessary funds for an abortion. If minors have to travel hundreds of miles to find an abortion provider in a state without a parental notification statute, then they may carry the pregnancy to term. If women must see a physician twice and wait at least 24 h between visits before a procedure can go forward, then her termination is likely to be delayed. Measuring the impact of these policies on births is more challenging. Statistical power is limited. If the birth rate is approximately 3to 4times the abortion rates, then even a 10% decrease in abortion would at most result in a 2.5% increase in births. If some women respond to the new law by avoiding pregnancy, the increase will be even less.
The small change in births induced by these policies makes it very difficult to detect changes in health associated with each. The finding from studies report changes in suicide, maltreatment of children, and homicide associated with these laws are implausible. The reduced-form strategy used in many of these studies is vulnerable to omitted variable bias. One researcher, for example, reports that Medicaid restrictions increase suicides among women but mandatory delay laws protect against suicide. Two other economists report an increase of 30–60% in child abuse victims associated with mandatory delay laws. The rationale is that mandatory delay laws result in more unwanted children, but they never show that mandatory delay laws increase birth rates. Another study found that PI laws increase rates of gonorrhea among women less than 20 years of age compared with women 20 years of age and older from 1981 to 1998. However, it has been difficult to show that PI laws had any impact on abortion rates in the 1980s and the early 1990s and so any effect of sexually transmitted diseases is suspect. Moreover, data on sexually transmitted diseases by race are poorly reported in the US. In large racially diverse states, race was unknown in 30–40% of reported cases of gonorrhea.
In the next section the issue of abortion and health will be taken up but with the next generation of studies. The research designs improve. There is more attention to the credibility of the ‘first-stage’ and the quality of the instruments. The underlying theory can still be traced to the quantity–quality model of household production, but there is less interest in theory and more emphasis on the empirics.