This study estimates the effect of welfare reform on adolescent behaviors using a difference-in-differences approach. After defining the prereform and reform cohorts and considering the life course development of adolescent behavior by following each cohort from age 14 to age 16, we compare the welfare-target and nontarget populations in the two cohorts. The difference-in-differences estimates are obtained using an event history model. Our analysis suggests that welfare reform has not reduced teenage fertility and school dropout. We find modest evidence that welfare reform is associated with higher risk of teenage births for girls in welfare families and higher risk of school dropout for girls in poor families. A combination of a difference-in-differences approach and a life course perspective can be a useful way to delineate the effect of societal-level change on family phenomena.
Key Words: difference in differences, school dropout, teenage childbearing, teenage pregnancy, welfare reform.
Most of the attention paid to the Personal Responsibility and Work Opportunity Reconciliation Act (PRWORA), commonly known as welfare reform, has focused on mothers' transitions from welfare to work and on the time limits, sanction, and work requirements instituted to promote this transition. Improving the well-being of children and adolescents, however, was an important subsidiary goal of PRWORA. This was most notable in the case of adolescent childbearing and school enrollment. The legislation requires teenage mothers under the age of 18 to live with their parents and to remain in high school if they had not yet graduated in order to obtain welfare benefits. It also allows states to deny additional benefits to mothers of any age who bear a child while already receiving welfare to reinforce the disapproval of nonmarital births. But welfare reform also brought changes that could have increased the risk that adolescents bear children or drop out of school. Mothers' transition to work can change a family's daily routine dramatically, impose stress on adolescent children, and reduce the amount of parental supervision, particularly between the end of school and dinnertime, when adolescents may engage in high-risk behavior. Thus, the direction of change in adolescent behaviors cannot be determined a priori.
In this article, we examine data on two cohorts of young women to determine what changes, if any, in childbearing and school dropout appear to be associated with the experience of welfare reform. Welfare reform can directly influence adolescents through its implicit message of strong disapproval of unmarried childbearing and welfare dependency, which, if internalized by adolescents, may change adolescents' childbearing and school behavior. Indirectly, welfare reform can influence adolescents through family changes. On the one hand, the transition off welfare to employment may increase family income and mother's self-esteem, which may reduce the risk of teenage fertility and school dropout. On the other, the sudden reduction of mother's home time may reduce parental supervision and control, which may heighten the risk of teenage fertility and school dropout. Our data do not allow us to investigate the precise mechanisms by which welfare reform may affect adolescents' behaviors. Still, given the great changes in the welfare system produced by PRWORA, we argue that learning the direction and magnitude of change-whether PRWORA appears to have a positive or negative effect on childbearing and school dropout, and how large these effects are-is important to social scientists and policy makers.
Nonmarital births among adolescents appear to impose serious long-term consequences for the life chances of mothers and their children. Summarizing the research literature spanning 2 decades, by the late 1980s, the National Research Council concluded that women who become parents as teenagers are at greater risk of social and economic disadvantage throughout their lives than those who delay childbearing (Hayes, 1987). A revisionist school of research in the 1990s, however, claimed that the supposed consequences of adolescent childbearing merely reflected unobserved preconditions such as growing up in poverty (e.g., Geronimus & Korenman, 1992). Other researchers did not agree and showed that childbearing per se had statistically significant and quantitatively important effects on high school graduation, family size, and economic well-being after accounting for unobserved family preconditions (Huffman, Foster, & Furstenberg, 1993). Regardless of which is the real cause, teenage mothers are often not prepared for the emotional, psychological, and financial responsibilities and challenges of parenthood (Maynard, 1997). Many drop out of school and the majority do not return. Teenage mothers, it is argued, are vulnerable to a variety of undesirable outcomes, such as low socioeconomic attainment, high rates of unemployment, low wages, high rates of poverty, large family size, high welfare dependency, and lower prospects of marriage. Their children are said to be at greater risk of low cognitive and emotional development.
Certainly, many federal and state policy makers believe that nonmarital childbearing at any age is detrimental. The PRWORA legislation includes language stating that "the negative consequences of an out-of-wedlock birth on the mother, the child, the family, and society are well documented," followed by a list of negative outcomes. The legislation states further that "prevention of out-of-wedlock pregnancy and reduction in out-of-wedlock birth are very important Government interests" (see H.R.3734, the Personal Responsibility and Work Opportunity Reconciliation Act of 1996). Many policy makers also think that the pre-PRWORA welfare system encouraged nonmarital childbearing. They argue that the welfare system prior to PRWORA encouraged nonmarital births by offering timeunlimited benefits that made it easier to raise a child outside of marriage and also decreased social disapproval of nonmarital childbearing (Blank, 2002). Under PRWORA, it is argued, time limits, work requirements, and special provisions for adolescents could change the incentives, increase social disapproval, and thereby reduce nonmarital births. With respect to adolescents, PRWORA prohibits states from spending Temporary Assistance for Needy Families (TANF) funds on minor, unmarried, custodial parents who do not live at home or in an adult supervised setting; it also prohibits states from spending TANF funds on teenage parents who are not participating in high school or other equivalent training. TANF is the successor program to Aid to Families with Dependent Children.
RESEARCH ON WELFARE REFORM AND FERTILITY AND CHILD WELL-BEING
Academic research on welfare effects before waivers suggested that the level of welfare benefits has a real but modest effect on nonmarital fertility (Moffitt, 1998). But Blank (2002) pointed out that the previous finding of a small welfare incentive effect on fertility does not rule out the possibility that the sweeping changes implemented under PRWORA could produce a larger effect of welfare reform on fertility. The more recent research literature, which includes studies using nonexperimental and experimental designs, has not yet provided a consensus (see a review in Blank, 2002). Fein (1999) found few effects on fertility from a strong mandatory work activities program. Quint, Bos, and Polit (1997) found an increase in the teenage pregnancy rate under a program that provided educational and job assistance to teenage welfare mothers. Yet, by comparing the fertility rates of teenagers by age 17 or 19 between the early 1980s and the late 1990s, Kaestner, Korenman, and O'Neill (2003) found that welfare reform was associated with reduced fertility among young women in disadvantaged families. Offner (2003) found that welfare reform had a significant, small negative effect on the fertility of young women in lowincome families by comparing the pooled cross-sectional fertility rate of teenagers aged 14 to 19 during 1989-1992 with the comparable rate for those aged 14 to 19 during 1997-2001.
There is also a lack of consensus on the consequences of PRWORA for other indicators of child and adolescent well-being. Proponents believe that welfare reform can benefit children and adolescents because maternal employment may increase income, provide a good role model, and stabilize parenting. Opponents of welfare reform fear that welfare mothers may not be able to find a stable, decent-paying job and will have little time to supervise and discipline their children, with negative consequences for their developmental outcomes. The rationales underlying these debates involve family processes such as the allocation of time and material resources, role modeling, parental control and supervision, and parenting practices, through which welfare reform affects mothers' behavior and, in turn, child and adolescent outcomes.
The first source of evidence comes from nonexperimental studies, which are inconsistent. Coley and Chase-Lansdale (2000) and Peters and Mullis (1997) found support for the beneficial effect of welfare participation for adolescents, particularly for Blacks, whereas Ku and Plotnick (2003) found negative effects of welfare participation on adolescents' educational attainment. Bianchi (2000) found that maternal employment did not affect children's development, whereas Waldfogel, Han, and Brooks-Gunn (2002) found a negative effect of maternal employment during infancy for White children. Paxson and Waldfogel (2003) found that stricter time limits and tougher sanctions were related to an increase in child maltreatment. Kaestner and colleagues (2003) and Offner (2003) found that welfare reform was associated with a reduction of teenage dropout rates. Based on a longitudinal survey of a random sample of low-income families in low-income neighborhoods of Boston, Chicago, and San Antonio, Chase-Lansdale and colleagues (2003) found that mothers' welfare and employment transitions between 1999 and 2001 were not associated with negative outcomes for young adolescents aged 10 to 14. There was modest evidence of positive associations between mothers' employment and welfare transitions, on the one hand, and young adolescents' mental health and cognitive development on the other. An examination of the mechanisms through which mothers' employment and welfare transitions affect young adolescents suggested that increased income and little change in time with young adolescents might be the explanation. The authors tested whether the welfare and employment transitions had interaction effects and found none. This indicated that there was no significant difference between welfare families and nonwelfare low-income families. The evidence from this study does not fully support either proponents' or opponents' argument, with moderate evidence leaning toward the proponent's argument.
Another source of evidence comes from studies of child outcomes measured in random-assignment, antipoverty demonstration programs. Researchers at Manpower Demonstration Research Corporation (MDRC) conducted a meta-analysis of eight experimental-design employment demonstration programs-most begun before welfare reform was enacted-that involved some combination of welfare time limits, earnings supplements, and mandatory employment activities (Gennetian & Miller, 2002). They found few negative associations between leaving TANF-like demonstration programs and the health and well-being of preschool and school-age children. They found modest but statistically significant negative effects of the experimental treatments on teenagers' school performance, however.
The sociological literature on teenage pregnancy, birth, and school dropout has identified individual-level factors that increase the risk of teenage pregnancy, birth, and school dropout. These include family background factors such as ethnicity, family income, parental education, family structure, and number of siblings (Hardy, Astone, Brooks-Gunn, Shapiro, & Miller, 1998; Wu, 1996; Wu & Martinson, 1993). Parental welfare participation is another microfactor worthy of attention. Findings from studies examining how maternal welfare receipt affects daughters' fertility are contradictory. Gottschalk (1992) found that maternal receipt was a risk factor for premarital births, whereas Haveman and Wolfe (1994) found no association between them.
ISOLATING THE EFFECTS OF WELFARE REFORM
Welfare reform is a societal-level factor that targets a particular population with a high risk of welfare receipt. Isolating the effects of welfare reform on the target population presents a methodological challenge to researchers. We address four aspects of this challenge: period effects coincident with welfare reform, constructing a counterfactual for the target population under welfare reform, persistent societal factors producing differences between the target and nontarget populations, and the life course development of adolescent behavior.
First, welfare reform must be isolated from other period effects coincident with welfare reform, such as the economic boom of the mid to late 1990s. Most research to date on the welfare effect on adolescent outcomes has focused on welfare families (Gennetian & Miller, 2002; Morris, Houston, Duncan, Crosby, & Bos, 2001) and lowincome single-mother families (Chase-Lansdale et al., 2003). Findings from this line of research are informative but still tentative because of a lack of comparisons with the nontarget population so as to eliminate other period effects coincident with welfare reform. Other societal changes coincident with welfare reform, in other words, may affect the entire adolescent population in certain directions, whereas we would expect welfare reform to affect mainly the target population of low-income adolescents. Without an explicit comparison of effects on the target and nontarget population, researchers cannot be confident that they have identified a welfare reform effect. For example, if the findings from a study limited to lowincome adolescents shows a beneficial effect of welfare reform, there could be no welfare-specific effect if the nontarget population has experienced the same change. Similarly, a harmful effect inferred from a study based only on the target population might be spurious if the same harmful effect is also found for the nontarget population. Even if findings based on only the target population show no effect, there might actually be a beneficial or harmful effect depending upon what the nontarget population experiences. The effects of welfare reform must be isolated from other social changes taking place in the same period and affecting the target and nontarget populations alike.
Given sweeping national declining trends, this challenge to the interpretation of cause and effect is relevant to studies of teenage pregnancy and childbirth such as ours. According to the U.S. Department of Health and Human Services (2001a), teenage pregnancy rates steadily declined from 1990 to 1997 (the figure for 1997 is the most recent estimate), and the rate for young teens (aged 15 to 17) in 1997 reached the lowest level since 1980. The declines occurred across racial-ethnic groups. Teenage birth rates also underwent a steady decline from 1993 to 2000, and in 2000, the rate for young teens reached the lowest point since 1976 (U.S. Department of Health and Human Services, 2001b). All racial-ethnic groups experienced declines. The declines in teenage pregnancy and birth rates could be linked to changing attitudes and better contraception; many public and private efforts have focused teenagers' attention on the importance of pregnancy prevention through abstinence and responsible behavior (U.S. Department of Health and Human Services, 2001a). The declines might also be attributed to the introduction of new, easier to use, effective birth control methods (e.g., injectable and implanted longacting hormonal methods) adopted by some sexually active teenagers. These changes could affect all teenagers, and it is not surprising to see a declining trend across the board. Because it is difficult to quantify changes in attitude and behavior over time in order to isolate them from welfare reform, making a comparison between the welfare target and nontarget populations becomes a crucial means to evaluate the welfare reform effect on teenage pregnancy and childbirth.
The trend for school dropout rates is less clear (U.S. Department of Education, 2003). The status dropout rate, defined as the percentage of individuals aged 16 to 24 who were not enrolled in a high school and had not received a high school diploma or obtained an equivalency certificate, was 12.1% in 1990 and 10.9% in 2000, with year-to-year fluctuations. The dropout rate for non-Hispanic Blacks remained higher than for non-Hispanic Whites, whereas the rate for Hispanics was the highest and declined over the period noticeably. State policies on high school graduation requirements may increase dropout rates and explain the fluctuation in the trend. Because these policies apply more to later graduating classes than earlier graduating classes (U.S. Department of Education, 2002), we need to separate the graduation requirement policy from welfare reform.
Second, to isolate the welfare reform effect requires consideration of the counterfactual question, what would have happened to the target population had it not been subjected to welfare reform? Would it have still shown the same changes? In other words, the counterfactual of observing the target population in the reform era would be to observe the same population under a situation where the reform had not been implemented. In experimental research, one can achieve this situation by randomly assigning some members of the population to receive the experimental treatment (e.g., welfare reform) and others not to receive the treatment. In nonexperimental research such as ours, one promising strategy is to observe a target population before the policy was implemented to approximate the counterfactual population. Thus, comparing an earlier birth cohort who experienced adolescence before welfare reform with a later birth cohort who experienced adolescence after welfare reform can help isolate welfare reform as an exogenous cause of change in their life course. This cohort-comparison model approximates an experimental design in that the later cohort experienced the "treatment" of being subject to PRWORA's rules and restrictions but the earlier cohort did not. This research design is similar to the cohort-comparison model of Hogan (1978) and Shanahan, Elder, and Miech (1997), according to whom the unique histories of birth cohorts arising from the age-specific conjunction of period events affect the life course of individuals.
Third, to isolate the welfare reform effect, one must eliminate differences between the target and nontarget population due to persistent societal factors. Examples of these factors include the structure of the low-wage labor market, the volume of immigrant flows, and the social acceptance of multiple forms of family structure. To accomplish this objective, we use a double-comparison (or difference-in-differences) model. We first compare the target and nontarget populations within each cohort on rates of pregnancy, birth, and school dropout. This comparison yields differences in rates within each cohort. Then we compare the difference within the first cohort to the difference within the second cohort. If persistent societal factors have not changed over time, we can interpret a change in the size of the difference to welfare reform. Thus, the difference-in-differences method controls for unmeasured factors that create differences between the target and nontarget populations and that remain the same during the entire observation period. Its main limitation is that it does not control for unmeasured factors that change during the observation period. When the two cohorts are close enough, the unmeasured factors are more likely to remain the same, and the difference-in-differences model can eliminate their contributions. If too much time elapses between the two cohorts, it is more likely that these factors could change and therefore confound the identification of the welfare reform effect. For example, Kaestner and colleagues (2003) compared outcomes of teenagers aged 17 to 19 between the early 1980s and the late 1990s. The long period of time that elapsed between the cohorts, however, increases the likelihood that other historical differences may confound their estimates of the effects of welfare reform.
Finally, to isolate the effect of welfare reform on adolescents' behavior, we use a life course perspective. The life course perspective suggests that studying social change requires observations on two cohorts over the same life course stage before and after the change takes place (Elder 1994). Teenage girls at the onset of puberty enter a new life course stage in which they are at high risk of pregnancy, childbearing, and school dropout. Even if welfare reform produced stronger social disapproval of teenage childbearing and lower expectations of public transfers, it would take time for teenagers to internalize these messages and to alter their behaviors in response. Teenagers who entered this life course stage prior to welfare reform may have internalized a weaker social disapproval of teenage childbearing, which continues to expose them to higher risk of pregnancies, births, and dropout even though they experience welfare reform later in the same life course stage. By the same logic, the numerous public and private efforts to prevent teenage pregnancy that occurred before welfare reform may have changed the attitudes of teenagers who entered this life course stage prior to welfare reform, resulting in a lower risk of pregnancies, births, and dropout. Thus, we define the earlier cohort as spending the life course stage spanning the 36 months from age 14 to age 16 in the prereform era, and the later cohort as spending the same stage in the reform era. This approach can better isolate the welfare reform effect than the approach of comparing pooled cross-sectional rates before and after welfare reform used in Kaestner and colleagues (2003) and Offner (2003).
In sum, a difference-in-differences approach helps to address four aspects of the challenge of isolating the effects of welfare reform. The difference-in-differences in rates between the target and nontarget populations in the two cohorts can plausibly be ascribed to the experience of PRWORA, after adjusting for measured individual factors (e.g., race, parental income) that vary by individuals within cohorts, and measured environmental factors (e.g., state-level abortion regulations) that vary across states and over time. Consistent with previous research showing that disadvantaged family background is associated with teenage pregnancy, birth, and dropout, we consider low-income, single-mother family structure, parental welfare receipt, low parental education, and Black race as indicators of target population in our analysis.
This article assesses the effect of welfare reform on teenage pregnancy, childbirth, and school dropout using a nationally representative longitudinal survey, the National Longitudinal Survey of Youth, 1997 (NLSY97). It comprises a nationally representative sample of 8,984 individuals born in between 1980 and 1984, with an oversample of Black and Hispanic youth. Out of the 8,984 respondents, 4,385 are girls, and a subsample of them is used in our analysis (more detailed information is presented below). The NLSY97 has administered four annual interviews to the same individuals from 1997 to 2000. The initial response rate at first round is 91.6%. The retention rate is 93.3% at the second round, 91.4% at the third round, and 89.9% at the fourth round; the main reason for noninterview is refusal. In addition to the prospective information from the four interviews, retrospective fertility and enrollment histories were collected for all respondents so that we are able to establish pregnancy, birth, and school dropout histories from age 14, spanning the years 1994 to 2000. The NLSY97 sample of adolescents born between 1980 and 1983 allows us to define two cohorts by birth cohorts. Further, because the nationally representative sample includes the nonpoor, it allows us to compare the welfare reform effect between the welfare target population and nontarget populations. Using the difference-in-differences approach, we are able to plausibly isolate the welfare reform effect from effects of other societal changes on behaviors over 36 months of the same developmental stage under two policy regimes.
Defining the Two Cohorts
Defining the two cohorts depends on the definition of when welfare reform began. We argue that the effective dissemination of the messages of welfare reform (e.g., disapproval of unmarried childbearing) occurs through the actual state TANF welfare programs. Therefore, our operational definition of the start of welfare reform is the actual implementation month of the TANF programs in the respondents' residential states. We observe two cohorts of adolescents from age 14 to age 16, the first cohort during the prereform era and the second cohort during the reform era. The assignment of respondents to the two cohorts is according to the birth year and the actual implementation month of the welfare reform programs in their residential states. The reform cohort was born in 1982-1983 and subject to welfare reform programs over the life course stage from age 14 to age 16. The prereform cohort was born in 1980 and passed the same life course stage before welfare reform programs were implemented. Welfare reform is then the treatment. The reasons for choosing ages 14 to 16 are twofold. First, most girls have reached puberty by age 14 and have started a new developmental stage in which they are at risk of pregnancy, childbirth, and school dropout. Second, although it is ideal to include later adolescence (ages 17 to 19), the data do not allow us to do so. Among those who were born in 1980, the older ones reached only exact age 17 when the states started to implement the welfare reform programs. Among those who were born in 1982-1983 and reached age 14 after welfare reform started, the older ones also reached only exact age 17 at the last interview. We observe girls in the prereform cohort from exact age 14 and censor at exact age 17 or the implementation month of welfare reform programs of their residential states, whichever comes first (additional censoring criteria are used for different events; see more detailed description later). This cohort consists of 836 girls with an average of 31.8 months of observation. A more restricted criterion to define the prereform cohort is to keep those who spent their entire 36 months from age 14 to age 16 before welfare reform started, and to eliminate those who had not reached exact age 17 by the state implementation month. This reduces the sample from 836 to 278. Analysis based on this definition produced similar results as reported in this article. We observe girls in the reform cohort from age 14, which is always after the state welfare reform programs started, and censor at exact age 17 or at the month of the last interview, whichever comes first. This cohort consists of 716 girls with an average of 35.8 months of observation (10% of those born in 1982 and 72% of those born in 1983). The resulting sample of these two cohorts essentially excludes those respondents for whom the period from age 14 to age 16 spanned both the prereform and reform periods (e.g., those born in 1981).
The Quasi-Experimental Design
Our cohort-comparison model can be considered a quasi-experimental design. To understand the degree to which our quasi-experimental design can produce credible assessment of the welfare reform effect, we contrast it with a true randomized experimental design. According to Campbell and Stanley (1963) and Shadish, Cook, and Campbell (2002), three principles are the keys to a randomized experiment. First, the treatment group and the control group are randomly assigned so that their observed and unobserved characteristics are the same on average. Second, the treatment is independent of all environmental conditions and individual characteristics. Third, the control group is isolated from the treatment. We discuss below how closely our quasi-experiment approximates a randomized experiment in these three respects.
For the first principle, although our two cohorts are not randomly assigned (rather, they are defined by birth years and the timing of state welfare reform programs), individuals are not selected into the cohorts through their own choice. Because the timing of state implementation of PRWORA was unlikely to have been influenced by the characteristics of teenagers, we can safely assume that the timing of welfare reform does not lead to the problem of selection bias that is common in nonexperimental studies (Berk, 1983). The one obvious difference between the two cohorts is that persons in the prereform cohort were born in 1980, whereas persons in the reform cohort were born in 1982-1983. This birth cohort difference is unlikely to have created substantial differences between the two cohorts. Thus, we may view the two cohorts as two random samples of the population, approximating randomization.
To be consistent with the second principle, the treatment of experiencing welfare reform should be independent of environmental conditions and individual characteristics. Although it is fairly safe to assume that the implementation of welfare reform is independent of teenagers' characteristics, it is problematic to claim that it is independent of other state- or national-level characteristics and trends. Our design has two features to make this threat smaller. First, we use statistical controls for other state environments relevant to teenage girls' pregnancy, childbirth, and school dropout. In particular, we control for abortion regulations, the degree of paternity establishment, and unemployment rate across states and over years. As we mentioned before, not all coincident trends are quantifiable-for example, changes in adolescents' attitude toward sexuality and contraceptive use. These unmeasured national trends are still a threat to the credibility of a causal effect of welfare reform. This problem can be minimized by the second feature of our difference-in-differences approach. If the unobserved national trends such as attitudes influence the whole population, whereas welfare reform acts only on the welfare-target population, then the behavioral difference between the target and nontarget populations in the reform cohort should be different from that in the prereform cohort. Including an interaction term between the welfare reform period and an indicator of the target population (e.g., poor and nonpoor) will yield such a difference-in-differences estimate. With these two features, we hope to disentangle the welfare reform effect from confounding national and state environmental conditions.
For the third principle, the control group should be isolated from the treatment. Because the prereform group includes those who had passed ages 14 to 16 before welfare reform started, this principle is satisfied only if welfare reform had no influence on the prereform cohort. There are two reasons that this principle might not be completely satisfied, however. First, some states had received permission from the federal government before the passage of PRWORA to waive some of the existing welfare rules in order to try various work-incentive programs. Second, there was substantial publicity about welfare reform in the year or so before its passage. Both problems could have placed the prereform cohort under some degree of influence by welfare reform, even though the actual implementation of concrete welfare reform programs was more extensive and wide reaching than the waiver programs and publicity. Consequently, there still could be a treatment effect even if our statistical analyses do not find one. And if we do find a treatment effect, our estimate may be smaller than its actual magnitude. Future research using a prereform cohort 1 or 2 years earlier will help to clarify this issue.
In sum, we carefully approximated our quasi-experimental design to a randomized experimental design. Nonetheless, quasi-experimental studies cannot produce the exact policy effect that a randomized experiment can (Friedlander & Robins, 1995; Heckman, Ichmura, Smith, & Todd, 1998). Given situations where a randomized experiment is impossible (like ours), a careful design can reduce the bias; an understanding of the difference between a quasi-experiment and a randomized experiment will help to assess the direction of the bias.
The three events-pregnancy, childbirth, and school dropout-are the three dependent variables in our analysis. Using both prospective and retrospective data, we construct for the prereform and reform cohorts' three monthly histories: the pregnancy history (a repeatable event), the first childbirth history (a nonrepeatable event), and the school dropout history (a repeatable event). The event of pregnancy is defined as starting at the time of conception. We consider all pregnancies occurring during ages 14 to 16. We left-censored pregnancies occurring before exact age 14 and right-censored at first marriage or exact age 17. We delete the months when the individual was pregnant to avoid the influence of different duration of pregnancies due to miscarriage, abortion, and live birth, thus making the waiting time for the next pregnancy more accurate. First childbirth is defined as the date of birth, an event that is nonrepeatable; we left-censored persons with a birth before age 14 and right-censored at first marriage or exact age 17. The history is also censored after the first birth occurred. School dropout is defined as a spell of absence for at least three continuous months during a semester. Short-term dropout, which may be due to health problems and school transfers, is disregarded. Dropout is also a repeatable event. We right-censored at high school graduation or at exact age 17.
The key explanatory variable is welfare reform. Although the indicator for whether an observation is in the prereform or reform cohorts (the assignment to the two cohorts) is conceptually distinct from the indicator for the treatment (welfare reform), the measurement of the two indicators is the same. Thus, the indicator for welfare reform takes the value of 1 for all of the observations of the individuals in the reform cohort, and 0 for all of the observations of the individuals in the prereform cohort.
Social environments other than welfare policy facilitate or constrain the behaviors of adolescents. Joyce and his colleagues (Joyce & Kaestner, 1996; Joyce, Kaestner, & Kwan, 1998) demonstrated that stricter abortion regulations suppressed fertility behavior. To separate welfare reform from this state-level environment, we measure abortion regulations using information from the National Abortion and Reproductive Rights Action League. Abortion regulations vary across states and years. An index of abortion regulations is created based on three items: (a) waiting hours (ranging from 0 to 60), (b) parental consent, and (c) reasons for public funding (life endangerment, rape/incest, health circumstances, and most circumstances). Higher values of the index indicate more strict regulations. Strict enforcement of child support obligations appeared to depress births outside marriage (Case, 1998). The strictness of child support enforcement varies by years and by states. We construct a paternity establishment index made up of the proportion of all nonmarital births that have established paternity and the per-birth expenditure in laboratory paternity establishment. The data are drawn from the Department of Health and Human Services (2001). Because the years 1994-2000 evidenced a strong economic boom, we used state unemployment rates to control for the state economic structure that might confound the welfare reform effect. Data were obtained from the Bureau of Labor Statistics. The Department of Education (2002) provides data on the number and distribution of required courses, minimum competence tests, and the first graduating class to which these requirements apply. For our purposes, to separate the effects of state graduation requirement policy from the overlapping effect of state welfare programs, we focus on a time-varying measure. We measure state graduation requirement policy using a dummy variable, with the value of 1 beginning in the year in which the first graduating class was affected.
Our study includes variables at the individual/ family level such as age in months, race and ethnicity (White, Black, Hispanic), family structure (intact, step, single-mother, other), parental family income-to-needs (family income adjusted by the poverty line for that family in a particular year), parental education (highest between the two parents), parental welfare receipt (receiving AFDC before 1993, between 1993 and 1997, no information about parental welfare receipt after 1997 in the NLSY97), number of siblings, and urban residence. Race and ethnicity, parental education, and parental welfare status are time-invariant, and all others are time varying. Among the family background variables, indicators for 130% of poverty line, single mother, and parental AFDC during 1993-1997 are used to identify the welfare-target population. In addition, we include two other indicators: low parental education and Black families. The purpose of adding these two stable (time-in variant) indicators is to reduce the influence of the unstable (time-varying) nature of the former three indicators. Low parental education (without a high school education) and Black background are two disadvantaged family backgrounds leading to greater probabilities of poverty, single motherhood, and welfare participation.
Table 1 compares the crude rates of the three events for the two-cohort sample, the whole sample, and the general population. The average pregnancy rate for ages 14 to 16 is 5.3% for the prereform cohort and 4.1% for the reform cohort. These rates are relatively higher than the rates for the whole sample in 1997 and 2000 for the same age groups, respectively. Because the rates for ages 14 to 16 are not available in the national statistics, we compute the rate for the age group 15 to 17 for the whole sample: The NLSY97 rate in 1997 is 6.3, similar to the national statistics (6.4). Pregnancy rates for later years are not available in the national statistics. Turning to teenage birth rates, we see a decline from the prereform to the reform cohorts, consistent with the NLSY97 whole sample rates and the rates reported in the national statistics. The last two columns show the dropout rates. Unlike the pregnancy and birth rates, the dropout rate increases from the prereform cohort to the reform cohort, consistent with the rates for the entire NLSY97 sample. The age group for the national dropout rate is 16 to 24, only overlapping at age 16 with the NLSY cohort sample and total sample. The national dropout rate for age 16 in 2000 is similar to the NLSY97 rate, but the national rate for ages 16 to 24 remains similar from 1997 to 2000.
Table 2 compares the event rates across different family backgrounds as alternative indicators for the welfare-targeted population and shows the between-cohort difference and its significance level. The teenage pregnancy rate is higher for girls with disadvantaged backgrounds. It declines from the prereform to the reform cohort for the total sample, for those with low parental education, and for Blacks. Similarly, the teenage birth rate is higher for girls with disadvantaged backgrounds. There is no significant decline between the two cohorts, however-neither for the total, nor for the subgroups. Although it is also true that the school dropout rate is higher for individuals with disadvantaged backgrounds, the rate increases from the prereform cohort to the reform cohort for the total sample, the poor, and Blacks.
Table 3 presents the descriptive statistics for individual-level characteristics between the prereform and reform cohorts. We focus on whether the two cohorts are comparable on individual/ family characteristics. Because the two cohorts have the same life course stage (ages 14 to 16) and a similar number of follow-up months, the age distributions of the two cohorts are almost identical. Similar distributions also characterize family structure, parental family income, parental education, and parental AFDC status. Other variables show systematic differences. The prereform cohort consists of more minorities, fewer missing income cases, a smaller number of siblings, and a larger proportion living in urban areas. These differences are not large in magnitude, and we hope that controlling for these variables in the multivariable analysis will improve the comparability between the two cohorts.
We present the distribution of state-level variables in Table 4 where state-months are the observation unit. We do not use the person-month data to avoid unbalanced contributions of sample individuals to different states. Along with the continuous strong economic boom, the state unemployment rate declines between the two cohorts from 5.34 to 4.18. The abortion regulation index for the period 1994-2000 has a mean of zero and a standard deviation of .73. The abortion regulations are slightly tightened for the reform cohort (increased by about one tenth of a standard deviation). The index for paternity establishment enforcement has a mean of zero and a standard deviation of .85. The enforcement is much stronger for the reform cohort than for the prereform cohort (about one third of a standard deviation). The proportion of months lived under the state graduation requirements is smaller for the prereform (0.35) cohort than the reform cohort (0.53). These state environments are very likely to confound the welfare reform effect for teenage pregnancy, childbirth, and dropout. The state-varying and time-varying measures of these environments make it possible to separate them from the indicator of welfare reform in the multivariate analysis, to which we now turn.
Table 5 reports the logit estimates of the baseline model for the three events. The baseline model does not include the interaction term between the indicator for welfare reform and an indicator for the welfare-target population (the difference-in-differences estimator). The purpose of the baseline model is to estimate the effects of individual/family characteristics and other state-level environments on the three events under study before turning our focus to the welfare reform effect. Logit coefficients (log-odds) and their standard errors are presented.
The first column lists estimates for teenage pregnancy. As teenagers grow older, they have a greater risk of pregnancy. Nonintact families, including stepfamilies, single-mother families, and other family types, as well as earlier parental AFDC status, are risk factors for teenage pregnancy. The estimate for the indicator of welfare reform has a negative sign but does not reach the 0.05 significance level. This indicates that welfare reform, together with the coincident period effects, such as attitudes toward teenage sexuality and contraceptive use, do not significantly reduce the risk of teenage pregnancy for the whole population.
Estimates for teenage births are found in column 2. As was the case for pregnancy, the risk of having a birth increases with age. Stepfamilies, other family types, and low family income are found to be significant risk factors. Stronger enforcement of paternity establishment induces a greater probability of having a birth. Although past research has found a suppressing effect of child support enforcement on nonraarital fertility for adult women, it is possible that paternal responsibility provides teenage girls a workable option to give birth to a child instead of aborting their pregnancies. Welfare reform, together with all coincident period effects, does not reduce the risk of teenage birth for the whole population.
Turning to school dropout in column 3, aside from age being a risk factor, other types of family structure and earlier parental welfare status are two risk factors at the individual level. Welfare reform and other simultaneous societal changes significantly increase the risk of dropping out of school for the whole population. Whether welfare reform alone, disentangled from other simultaneous societal changes, decreases or increases the risk of each of the three events will be seen in the difference-in-differences estimates to be presented below.
The standard errors of coefficients in Table 5 are robust estimates, which take into account that repeated monthly observations within an individual are not independent. The bottom of Table 5 presents the Wald [chi]^sup 2^ tests of the current model against a model with only the constant, all of which are significant. As found in the past research, however, models for these events do not have a great deal of explanatory power, and only a few predictors are statistically significant. Because state environments are an important level of influence, we estimated an extended model (results are not shown here) that included state random effects; that is, we decomposed the error term into two components: one at the state level and the other at the individual-month level. We tested and found that the variance of the state-level error component was not different from zero. Therefore, we did not proceed further to a state fixed-effects model. We concluded that a simpler one-level model (the one presented here) fits as well as a two-level model.
Five sets of difference-in-differences estimates are presented in Table 6. For each indicator, we present the coefficient for the main effect of welfare reform ([beta]^sub 1^) and the interaction effect ([beta]^sub 3^), which is the difference-in-differences estimate of the welfare reform effect. A statistically significant interaction coefficient indicates that welfare reform has an effect on the target population. We use several potential measures of the target population: poverty, single mother, parental AFDC status, low parental education, and Blacks. For all three behaviors and for all indicators of disadvantaged family backgrounds, none of the estimates for the interaction terms is negative and significant, providing evidence that welfare reform does not reduce teenage fertility and school dropout as intended. The estimates are all insignificant for teenage pregnancy (column 1), and all but one is insignificant for teenage birth and school dropout with the lone significant estimate in each case in the opposite direction (columns 2 and 3). For teenage births (column 2), we detect a positive interaction effect with parental AFDC. This implies that welfare reform may increase the risk of teen births for girls in welfare families, which is the opposite effect of what welfare reform's supporters expected. Column 3 suggests a harmful effect of welfare on school dropout for low-income girls. Because we do not find significant, positive effects on teenage births and school dropout in other disadvantaged family backgrounds, we conclude that the evidence of an unintended welfare reform effect is sporadic and limited, subject to further research.
Thus far, we have not found evidence that welfare reform has succeeded in reducing teenage fertility and school dropout. Because welfare reform has granted states great latitude in designing their own welfare programs, there is large variation in the stringency of state welfare programs. A logical next step is to examine the welfare reform effect in states with high levels of stringency. Blank and Schmidt (2002) ranked states in three levels on four aspects of their welfare programs: benefit generosity, earning disregards, sanctions, and time limits. We combine this information into three categories of stringency. A high level of stringency means tougher sanctions, shorter time limits, less generous benefits, and smaller earning disregards. Repeating the analysis in Table 6 for the subsample living in high-stringency states led to the similar results as using all states.
The main objective of PRWORA was to encourage more welfare-receiving mothers to leave the rolls and obtain jobs. Changing the behavior of adolescents in families with high risk of welfare receipt, however, was an important subsidiary goal. Assessing the causal effect of such a nationwide change on the adolescent population raises a challenge to researchers. This study attempts to address several aspects of the challenge in order to arrive at a credible estimate of the welfare reform effect. First, there may be other societal-level changes occurring at the same time as welfare reform. If the other changes affect the whole adolescent population, however, then we may be able to isolate the welfare reform effect because it should affect only the target population. We followed this strategy by comparing the welfare-target and nontarget populations. Second, to isolate the welfare reform effect, we must be able to construct a counterfactual population. Under a cohort-comparison model, we use a cohort that did not experience welfare reform to approximate the counterfactual. Third, certain difference between the target and nontarget populations may have existed before welfare reform. Thus, we examined changes in the differences between the target and nontarget populations across two cohorts, which effectively eliminated time-invariant confounding factors. Fourth, adolescents may need time to learn the new rules or to internalize new norms promoted by welfare reform; therefore, the life course development of adolescent behavior must be taken into consideration. We followed two cohorts of teenagers from age 14 to 16 and estimated transition probabilities using an event history model. Taken together, our approach is a combination of a difference-in-differences model and a life course perspective. This approach is not common in family research but can be a useful way to estimate the plausible effect of societal-level changes on family phenomena.
For all three behaviors under study (teenage pregnancy, teenage birth, and school dropout) and for all five indicators of disadvantaged family backgrounds (low-income, single-mother, parental AFDC receipt, low parental education, and Black), none of the estimates of the difference in differences is significantly negative. None, therefore, suggests that welfare reform had its intended effect of reducing teenage fertility and school dropout. An additional analysis of individuals living in states with high levels of stringent programs led to the same conclusion. We detected sporadic evidence that welfare reform might have a harmful effect for adolescents in specific circumstances. Teenage girls in welfare families were more likely to have births in the reform era than those in the prereform era, and girls in low-income families were more likely to drop out of school. But because we did not detect the same harmful effect for other disadvantaged family backgrounds, these results are not conclusive.
Overall, then, we found neither consistent positive nor negative effects of welfare reform on teenage fertility and school dropout. The predominance of null findings is consistent with an observational study by Chase-Lansdale and colleagues (2003), which found that mothers' transitions off welfare and into employment were largely unrelated to changes in children's well-being. Our finding differs from those of Kaestner and colleagues (2003) and Offner (2003), however, who found that welfare reform appeared to reduce teenage fertility or school dropout. The harmful effects on adolescents found by the MDRC experiment studies (Morris et al., 2001) are consistent only with our sporadic findings.
Why might welfare reform have failed to affect teenage childbearing and school dropout? We cannot answer that question adequately with our data. If our findings are confirmed by other studies, likely mechanisms should be studied. We speculate, however, that welfare reform might reduce parental control and supervision of children who are at substantial risk of teen births and school dropout. Mothers who are at work during the day may not be able to monitor adolescent behavior during after-school hours; those who work the second shift may have similar difficulties in the evening hours.
Four limitations of our studies should be kept in mind. First, it is possible that the older cohort's behavior was influenced by the publicity about welfare reform during the year before its passage, or by the experimental programs some states undertook using waivers from the federal government. If so, we may have underestimated the effect of welfare reform-although publicity of a law is quite different from passage-and post-PRWORA programs are much more extensive than waiver programs. Second, our difference-in-differences estimator is not able to eliminate unobserved time-varying factors that may create differences between target and nontarget populations. Thus, it is possible that the estimated welfare reform effect is confounded by unobserved, time-varying factors beyond those already controlled (abortion regulation, paternity establishment, and unemployment rate). Third, our design does not examine mechanisms through which welfare reform may change adolescents' behavior. The estimates we produced represent a combination of the effects of mechanisms at the societal, family, and community levels. Last, the message of disapproval of unmarried childbearing and welfare dependency conveyed by welfare reform may take more time to reach adolescents. Although our design has allowed adolescents time to learn the new rules and norms from age 14, these new rules and norms may not come to their awareness until later ages. Therefore, our analysis may have missed the actual effect of welfare reform. Subsequent studies may include a longer lag time since the implementation of state TANF programs.
Although our data do not allow us to answer the question of why welfare reform may have failed to reduce teenage childbearing and school dropout, they do suggest that policy changes such as welfare reform can have complex effects on family life that are hard to predict a priori. A program to increase income and employment may change the home environments of adolescents in multiple ways: They may feel less anxious about their families' financial situations and may have parents with greater self-esteem (see Chase-Lansdale etal, 2003), but they may also receive less supervision on a daily basis and less monitoring of their school performance. We know, for example, that risky behaviors often occur in the after-school hours, when employed parents are not home (Lamer, Zippiroli, & Behrman, 1999; Steinberg, 1986). The net results of these sometimes offsetting factors is that a program may have no net measurable effect, as appears to be the case with teenage fertility and school dropout. Alternatively, many welfare-receiving mothers and their children may have such challenging daily lives that changes in the welfare system have less influence than policy makers expect. If confirmed by others, our results would suggest the difficulty of Grafting effective family policies on a large scale.
The research is supported by grant R01HD37018 from the National Institute of Child and Human Development and the Visiting Scholarship from the Russell Sage Foundation for the first author, 2002-2003.
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LINGXIN HAO AND ANDREW J. CHERLIN
Johns Hopkins University
Department of Sociology, Johns Hopkins University, 3400 N. Charles Street, Baltimore, MD 21218 (firstname.lastname@example.org).