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Preventing Subsequent Births to Welfare Recipients

Glenn C. Loury, Boston University

"I. Introduction The worth of any piece of evaluation research depends on its internal and external validity.  In the broadest sense, internal validity refers to the ability to rule out alternative interpretations of research findings, and external validity is the ability to support generalizations from findings to larger populations of interest. Both internal and external validity are promoted by three factors:

1.      Experimental and control populations in demonstration programs should resemble the welfare populations of interest and the circumstances each group will face, both with and without welfare reform.

2.      A program’s underlying design should adequately distinguish between competing hypotheses about observed outcomes.

3.      The implementation of a program should be carried out in a manner consistent with the program design.

 

This chapter summarizes the effectiveness of several programs to reduce subsequent births to women on welfare in terms of the validity criteria described above. The programs fall into three categories: direct or indirect monetary incentives; case management, often with enhanced services; and home visitation by nurses.

 Direct or Indirect Monetary Incentives

 One way to discourage additional births to welfare recipients is to impose a direct financial penalty, such as “capping” the benefit level, despite the greater family size that occurs when another child is born. Another approach, which uses indirect financial incentives, involves paying recipients to participate in activities aimed at reducing pregnancy.  Both direct and indirect monetary incentives have been used in a number of experimental programs in recent years, and we are now in a position to draw some tentative conclusions about their efficacy. The evidence does not support the view that policies relying primarily on financial incentives can significantly reduce subsequent pregnancies among welfare recipients.

Obviously, the impact of any program using financial incentives depends on the magnitude of the incentives involved. In the much-discussed “family-cap” experiment in New Jersey, for example, a welfare mother with two children faced the prospect of not receiving a scheduled benefit increase of $64/month (about $15 per week) in the event that she had another child. Indeed, in all the studies reviewed below, the financial benefits or penalties involved were quite modest. It is, perhaps, not surprising that direct incentives of this magnitude cannot exert much leverage over the choices people make regarding child bearing.

Nonexperimental Evidence
We turn now to a consideration of the evidence, beginning with an informative, nonexperimental study of the relationship between benefit levels and family size among welfare recipients. Fairlie and London (1997) sought to discover whether differences across states in the extent to which Aid to Families with Dependent Children (AFDC) benefits increase with family size tend to be causally related to differences across states in the rate of higher-order births among welfare recipients. Relying on monthly panel data from late 1989 to early 1992 taken from the Survey of Income and Program Participation (SIPP), their sample included women ages 15 to 44 with at least one child.

Initially, Fairlie and London (1997) focused on a subsample of AFDC recipients only. Controlling for a variety of individual characteristics, including race, they found that recipients living in states with higher incremental benefits were more likely to have additional children than recipients in less generous states. This initial finding suggests that a more generous supplement for greater family size does, indeed, encourage AFDC recipients to have more children. As Fairlie and London note, however, the causality could run in the opposite direction: states whose populations exhibit greater fertility (for reasons unrelated to welfare payments) may choose to provide more generous incremental benefits.

To test for such a possibility, they ran a cross-state regression on subsamples of the SIPP data consisting of people not receiving AFDC, whose behavior therefore would probably not be affected by cross-state variation in incremental welfare benefits. Fairlie and London chose three different comparison groups for this purpose:
1.      All single women who had at least one child but did not receive AFDC,

2.      A group defined by excluding from the first group the women who would ultimately receive AFDC, and

3.      A group defined by adding to the second group all married women who had at least one child and who did not receive AFDC.

In all three of the subsamples, they found the correlation across states between incremental AFDC benefits and higher-order birth rates to be statistically the same as in the original welfare-receiving population. This finding strongly suggests that the initially estimated large effect of incremental benefits on family size among AFDC recipients does not provide evidence of a casual relationship. Put differently, the nonexperimental data provide no support for the view that policy makers can prevent subsequent births to welfare recipients by lowering the benefit increases associated with additional births.

Family-Cap Experiments
This negative finding also is consistent with the experimental data generated by the so-called family-cap demonstrations. In New Jersey’s Family Development Program (FDP), AFDC recipients were precluded from receiving additional cash payments for a child conceived while on welfare (Camasso, Harvey, and Jagannathan 1996). This amounted to a loss of  $102 per month for a second child and, as mentioned earlier, $64 per month for any additional children. The FDP also provided supplemental employment, training, and education services for parents on welfare, reduced the disincentives for attending college and getting married, and established new rules that were more generous in providing Medicaid and limiting earnings reductions for those finding jobs and getting off welfare. In Arkansas, the Welfare Waiver Demonstration Project also included a monetary cap on benefits and a greater focus on family-planning services at intake and subsequent reevaluations (Turturro, Benda, and Turney 1997). Both states made an effort to compare the results for recipients subjected to these programs with the results for a control group of recipients not facing such provisions.

            The same outcome was observed in both programs (see tables 1 and 2): no significant difference in subsequent birth rates between experimental and control groups was found. Over the three-year waiver period of the Arkansas program, women in the experimental group averaged 0.16 births per recipient, and those in the control group averaged 0.14 births (Turturro et al. 1997). In the New Jersey program, 7.2 percent of the experimental group and 7.3 percent of the control group had a birth in the first year after the cap was imposed; 5.6 percent of the experimental group and 5.7 percent of the control group had a birth in the second year (Camasso et al. 1996).

It is tempting to draw the conclusion from these experimental data that family-cap policies have been proven not to work; however, we think some caution is warranted. To be sure, the data do not support the opposite view, but the implementation problems in these experiments were so severe that one may question whether family-cap programs actually have been fairly tested. For example, in the Arkansas Project, 46 percent of women in the experimental group and 52 percent of women in the control group indicated to program evaluators that they did not know how much more money they would receive if they were to have another child. Among those who thought they did know, disturbingly similar responses were found in the two populations: 17 percent of the experimental group and 11 percent of the control group thought they would receive nothing more; 6 percent of both groups thought the increment would be less than $45; and 2 percent of the experimental group (versus 10 percent of the control group) thought the increment would be $50 or more (Turturro et al. 1997). Obviously, financial incentives cannot affect the behavior of people who do not know what the incentives are!

This confusion may have resulted largely from misleading or inaccurate information provided by caseworkers. It turns out that at the beginning of the Arkansas project, 14 percent of the caseworkers were uncertain as to how clients were assigned to control or experimental groups. Only 7 percent of the workers knew that the experimental group differed from the control group in that they were subject to the cap on benefits and were to receive more intensive family-planning information and services. More than half of the caseworkers thought the treatment consisted only of the family cap; another 12 percent thought the treatment consisted only of increased emphasis on family planning (Tuturro et al. 1997).

            According to the Arkansas evaluation report, “both the experimental and control clients were given an explanation of available services by the caseworker (79%) and an offer of family-planning services (87%)” (Turturro et al. 1997, 21). This information was in accordance with the guidelines of the program. Yet, although only the experimental group was supposed to receive the brochure “Your Guide to Family Planning,” in fact only 24 percent of the caseworkers abided by this program requirement. Half of the workers gave the brochure to both groups, and the remainder gave it to neither (Turturro et al. 1997).  One may also wonder about the effectiveness of such written material with what is quite likely to be a low-literacy population.

The New Jersey FDP had similar implementation problems. The main duties of the caseworkers were to determine AFDC eligibility and to calculate benefit levels. About half of the workers also were responsible for assigning new applicants to experimental or control groups for the purposes of the family-cap demonstration.  This assignment process was supposed to be random; yet, more than one-quarter of the workers freely admitted to evaluation researchers that they used discretion in making assignments (Camasso et al. 1996). The responsibilities of case managers in the FDP program included “identifying the service needs of their clients, making referrals to these services for their clients, and monitoring clients’ participation in and progress through their activities” (Camasso et al. 1996, 32). When presented with five different hypothetical cases to test their understanding of the provisions of the program, the fraction of correct responses from case managers ranged from 30 percent to 54 percent.[1] It is evident that case managers were not adequately informed about the basic provisions of the program, especially with regard to the family cap.

It is therefore not surprising that participants did not have a good understanding of key provisions of the program. Only 39 percent of the actual control group members knew that they were in the control group, and only 65 percent of experimental group members correctly reported to evaluation researchers that they were subject to the new rules. (About 28 percent of the women in the experimental group thought that they were in the control group.) Although more than 80 percent of the experimental group members knew about the family-cap rule, as few as 25 percent knew about other important aspects of the program (Camasso et al. 1996). Because of these implementation problems, in neither the New Jersey nor the Arkansas programs were the experimental and control groups as different from one another as the evaluation design specified. The result is a severe problem of internal validity for these studies.

These studies also have problems of external validity. It is not clear that program participants should be taken as representative of the typical welfare population. A comparison of the initial sample of 992 program participants in Arkansas to the general Arkansas AFDC population showed that the former were more likely to have been previously employed, to have received higher AFDC and food-stamp payments, and to have been on AFDC longer (Turturro et al. 1997). The studies also experienced attrition problems: in Arkansas, Turturro and colleagues’ follow-up study two years after the initial survey included only 335 of the initial respondents. Response rates were similarly low for the New Jersey program. Out of the 3,303 attempted telephone contacts, only 1,238 were successful. Response rates were even lower for in-person interviews (21 percent) (Camasso et al. 1996). Furthermore, successful contacts did not guarantee completed interviews. Comparing survey respondents with the entire AFDC caseload, Camasso and colleagues found that survey respondents were (1) less likely to be high school dropouts (36 percent versus 46 percent), (2) less likely to be Hispanic (24 percent versus 30 percent), and (3) older (32 versus 28 years).

Moreover, the level of family-planning services actually provided to participants in these demonstrations was low, and differences between the control and experimental groups were small. In the Arkansas program, Tuturro and colleagues (1997) found that only about 20 percent of experimental group members received “Your Guide to Family Planning Services” (along with 5 percent of control subjects, who were not supposed to receive the pamphlet). Less than 5 percent of all clients in either the experimental or the control group were reported to have received other family-planning services. Tuturro and colleagues also found that the amount of time spent on the explanation and offer of services amounted to an average of less than two and a half minutes.

Thus, although experimental and control groups in both the Arkansas and New Jersey programs became pregnant at about the same rates, the problems of implementation and sample attrition at both sites were so severe as to preclude drawing strong conclusions. The evaluations fail to meet standards of internal validity because the similarity of services and information provided to experimental and control groups implies that the effective “treatment” was weak; therefore, one should expect to observe little or no effect from that treatment. (Part of this “weak treatment” problem was the result of the implementation problems described above, but in our view, it also resulted from a poor program design that allocated too little time for the provision of family-planning services.) Moreover, because of the “nonrepresentativeness” of the populations studied, care should be taken when generalizing the findings to the larger universe of interest.

In their final report, Camasso, Harvey, Jagannathan, and Killingsworth (1998a,b) updated the experimental analysis and added a pre–post analysis. Both analyses suggested that the family cap led to a decline in births and a rise in abortions. In his review of the Rutgers’ research, however, Peter Rossi concluded that problems with implementation, data collection, and statistical methods undermined the findings, so that “the various forms of evidence in the reports are not firm enough to support the researchers’ claims” (see Chapter X). For example, the final experimental study relied on administrative data rather than survey responses. This approach meant that the analysis did not include outcomes for mothers no longer enrolled in AFDC, thereby subverting the experimental nature of the evaluation. As Rossi points out: “This analytic strategy used meant that the major advantages of the experimental design were lost. Potentially large selection biases were possible, which could arise from enrollment changes subsequent to randomization.”

Similarly, the pre–post analysis was based on administrative data for the entire AFDC caseload from 1990 through 1996 (Camasso et al. 1998a,b) The researchers used multivariate analysis to compare preprogram trends in births, abortions, and other outcomes to trends after the implementation of the New Jersey FDP. Their findings suggested that the intervention reduced births and increased abortions. As with the revised experimental–control analysis, however, Rossi concluded that the “research design cannot support definitive estimates of the effects of a program.” In particular, he expressed doubt that the evaluation could adequately control for the effects of time and other forces that might have influenced outcomes and that the statistical models used were inappropriate in some cases.

The apparent weaknesses of the New Jersey evaluation led Rossi to conclude: “The New Jersey FDP may have had the effects that the Rutgers research group claim or it may not have had those effects. We simply do not know from this research. The difficulty is that the deficiencies noted above are serious enough to cast strong doubts upon the validity of the findings.”

Other research has gone beyond state-level demonstration projects to assess the impact of policies intended to reduce fertility among unmarried women on a national basis. Horvath and Peters (1999) examined the impact of welfare-reform waivers on nonmarital childbearing. They used Vital Statistics data to calculate the proportion of nonmarital births for each state from 1984 through 1996. They then ran a series of regression models that included a range of economic and demographic variables as well as variables reflecting whether states had requested, received, and implemented various waivers that could affect childbearing, including the family cap. They concluded that “welfare waivers have a negative effect on nonmarital birth ratios” and that the family cap was a useful tool in achieving this objective (Horvath and Peters 1999, 27). The Horvath and Peters (1999) study, however, has many of the weaknesses typical of a nonexperimental evaluation. No control group is exempt from welfare reform, so they are forced to rely on statistical models to sort out the effects of changing economic, demographic, and social conditions from those related to welfare reform. The degree of uncertainty surrounding the estimated effects from such nonexperimental analyses is therefore considerably greater.

Several reasons exist to be concerned about the reliability of Horvath and Peters’ (1999) data. For example, their nonmarital birth data are based on Vital Statistics, which in many states may be inaccurate. Marital status is generally determined by asking the mother at the time of completing the birth certificate, but during the study period, about half a dozen states (including California and New York) inferred marital status using other approaches. For example, some states still considered a mother unmarried if her last name was different from the father’s. If the number of mothers choosing to retain their maiden names increased during the period of the study, it would have introduced an upward bias in the reporting of nonmarital births.

Although Horvath and Peters (1999) used what appears to be a reasonable set of control variables in their analysis, they may nevertheless have omitted important factors that could have an important effect on fertility. Moreover, the specification of welfare waivers for statistical analysis is difficult and subject to considerable uncertainty (see, for example, Martini and Wiseman 1997). For example, as the New Jersey and Arkansas evaluations demonstrate, the implementation of a waiver does not guarantee that recipients were aware of the policy. If they were unaware of or did not understand the policy, their behavior may not have reflected the true effects of the desired intervention.

In addition, selection effects may exist, because the states that were most successful in reducing nonmarital births may have had particular, but unmeasured, characteristics that made them different from other states. For example, perhaps the states that were most committed to reducing welfare caseloads (and births to unmarried mothers) also were more likely to request welfare waivers. It may be that their commitment to changing the culture of welfare had more to do with observed changes in certain outcomes than the waivers themselves. Thus, the Horvath and Peters (1999) findings may be more suggestive of the impact of welfare reform writ large than of any specific waiver. Indeed, given the rapid social and programmatic changes now underway, it is unlikely that any nonexperimental analysis of welfare reform could disentangle the impact of multiple provisions, as this and other analyses purport to do.

Indirect Monetary Incentives
The family-cap interventions were not the only ones trying to reduce subsequent pregnancies by relying on monetary incentives. The Dollar-a-Day program used indirect financial incentives to induce adolescent mothers to participate in peer-group meetings designed to provide information about contraception and to underscore the importance of avoiding a repeat pregnancy (Steven-Simon, Dolgan, Kelly and Singer 1997). Participants included mothers under age 18 whose first-born child was younger than 5 months old. These mothers were recruited from the postpartum ward at University Hospital in Denver and from Colorado’s Adolescent Maternity Program at Children’s Hospital in Denver. The experiment was designed to test whether financial incentives could induce teen mothers to participate in peer discussions and whether such discussions, with or without financial incentives, could forestall subsequent pregnancies among these young women.

Participants were randomly assigned to one of four groups. The control group received only routine postpartum care with no interventions. The “incentive-only” group received $7 per week as long as they did not get pregnant, but the women attended no meetings. The “meetings-only” group could attend weekly gatherings of 10 to 15 peers and two adults, where the desirability and means of postponing future conception were discussed. Finally, a “meetings-plus-incentive” group gathered weekly for these discussions, with each participant receiving $7 at the meetings as long as she did not become pregnant. Out of 286 initial participants, 248 completed the final study interview. (This interview covered the 6 months preceding the diagnosis of a repeat pregnancy or the 24-month postpartum period, if no additional pregnancy occurred). Those not interviewed were distributed evenly across the four treatment groups and did not differ significantly from the others in age, socioeconomic status, or race.

As with the family-cap interventions, the outcomes from this experiment with indirect financial incentives provide no support for the view that such incentives, with or without peer-group meetings, are effective at lowering subsequent pregnancy rates. Indeed, the results were quite similar across the four different control and treatment groups (Steven-Simon et al. 1997; see table 3). About 9 percent of the participants conceived within 6 months of the birth of their first child, 20 percent within 12 months, 29 percent within 18 months, and 39 percent within 24 months. Participation in peer-group meetings was low: about 38 percent of the mothers in the experimental group did not participate in more than one of their group’s activities. It is noteworthy, however, that the “dollar-a-day” payments did seem to induce greater attendance at the peer-group meetings: although only 9 percent of the meetings-only participants attended one or more of their peer-group meetings, 58 percent of the meetings-plus-incentive participants did so. Yet, despite these differences, the pregnancy outcomes were the same for the experimental and control groups, even for the meetings-plus-incentive participants who went to at least half of their group’s activities during the first 6 months postpartum. 

Case Management
Rather than rely on financial inducements, a different approach to the problem of preventing subsequent births combines intensive case management with enhanced family-planning services to welfare recipients. We argue below that the experimental evidence does not encourage optimism about the effectiveness of this method, either. In practice, pregnancy prevention has been an ancillary part of these intensive case-management programs. The principle focus has been on improving the academic and vocational skills of the program participants, including Adult Basic Education and General Equivalency Degree (GED) preparation, pre-employment and occupational skills training, and job-placement assistance. Support services to facilitate participation in training activities have been provided in the form of childcare and financial help with transportation, training, and education expenses. Training and job-preparation efforts, not family-planning activities, accounted for the vast majority of client time and program resources in the case-management programs. Moreover, caseworkers and service providers have been reluctant to convey the clear and unequivocal value judgment that avoiding subsequent births is a good thing.

A leading example of the “case management with enhanced services” approach is the New Chance Demonstration. New Chance operated between 1989 and 1992 at 16 sites to assist women who had become mothers as teenagers, who were high school dropouts, and who were receiving AFDC. The objectives of the New Chance programs were
·       
to help program participants gain educational and vocational skills necessary to acquire good job opportunities and reduce their use of welfare,

·        to help participants postpone additional childbearing and improve their current parenting skills, and

·        to improve the cognitive, health, and socio-emotional outcomes for the participants’ children (Quint, Bos, and Polit 1997). 

To determine program effects, Quint and colleagues (1997) conducted evaluation interviews were conducted with randomly assigned experimental group and control group participants at the program start, at 1.5 years into the program, and again after 3.5 years. (Unless otherwise noted, information on the New Chance Demonstration is from the Quint et al. study.). The average age of sample members at the beginning of the study was 18.8 years. More than 90 percent had never been married, 65 percent had one child, and 27 percent had two children. About 52 percent were black, and 23 percent were Hispanic. Only 5 percent had completed 12 years of schooling, with the average highest grade equaling 9.9. Only 30 percent of the participants were reading at the 10th grade level or above, and one in five had never held a job. Participation in the program was voluntary. Most women chose to participate because the program provided a way for them to earn their GED and offered free day care.

The participants were randomly assigned to experimental and control groups. The experimental group was offered a wide variety of services, including instruction in basic academic skills, career exposure and employability development classes, occupational skills training, work experience, job placement assistance, health and family planning classes and services, parenting workshops, and life skills classes on communications and decision-making skills.  Within 18 months of program entry, the experimental group members each had participated for an average of about 296 hours in the activities. Adult education occupied the bulk of this time; women spent most of their time in ABE/GED preparation (101 hours on average), followed by skills training (67 hours), work internship (28 hours), employability development (26 hours), life skills (20 hours), and parenting education (18 hours). Only about 6 of the 296 hours of service delivery were devoted to family planning (Quint et al. 1997). Clearly, then, preventing subsequent pregnancies was not a major focus of the New Chance Demonstration program.

The family-planning activities included education classes or workshops held at least once a month, individual counseling, and providing information about other family-planning service providers. The intensity of these activities, however, varied across sites. For example, in their evaluation, Quint and colleagues (1997) reported that

 at a number of sites, case managers did not routinely or effectively counsel participants about their use of contraceptives. Some case managers resisted this role because they were uncomfortable dealing with the subject of sexuality or felt that they lacked the requisite expertise. Still others were comfortable with the subject but, given the limited time they had to spend with each participant, tended not to discuss family planning unless the young women raised it as a specific problem. (pp. 74–75)

 

Members of the experimental group were much more likely than control group members to have attended previous family-planning classes (55 percent versus 20 percent) and to have received personal counseling (48 percent versus 24 percent) (Quint et al. 1997). After 42 months, however, they had not fared any better than control subjects in experiencing a repeat pregnancy (about three-fourths of participants), or in having a subsequent birth (about one-half of participants) (see table 4). Indeed, Quint and colleagues found that women in the experimental group were slightly higher along these dimensions, although the differences were statistically insignificant. The findings were fairly uniform across sites (all of which varied in the intensity of the family-planning activities), the only exception being that those who attended more than 10 family-planning sessions were somewhat less likely to have given birth.

The problem with drawing policy conclusions from this study is the probable failure of external validity. Both experimental and control group members were chosen from volunteers who sought out the program, rather than from welfare recipients who were assigned to the program without choice.  Those who aggressively seek GEDs and other training opportunities may well differ from those who do not, having more education, greater motivation, fewer socioeconomic disadvantages, and lower rates of mental illness and drug addiction.  To see why this is a serious concern, note the pronounced differences reported in the evaluation between the control group members in the (voluntary) New Chance program, and the teen parents in the (mandatory) Ohio program, Learning, Earning, and Parenting (LEAP): Whereas only 15 percent of the LEAP parents not enrolled in school at the beginning of the study had participated in vocational training at the end of the third year follow-up, more than 34 percent of the New Chance control group members had participated in similar skills training (Quint et al. 1997). The selection problem may be especially severe in this case: follow-up studies found New Chance control group members to have higher levels of education and training participation than did the control participants in other programs that relied on volunteers, suggesting that they may have been an especially select group. Because of this selection bias problem, differences between experimental and control group members in the New Chance Demonstration might understate the effectiveness of the intervention.[2]

In addition to these selection issues, the voluntary character of the program meant that the level of services received by experimental group participants may have been artificially low as a result of poor attendance and early departures from the program. Consider the distribution among participants of the hours of service received: although 22 percent received more than 500 hours of service, more than one-third received 100 hours or less, the equivalent of 17 days of GED instruction, 11 days of skills training, and 4.5 days each of work internship and employability development (Quint et al. 1997). The average level of participation in other activities was similarly limited.

Another program, the Teenage Parent Demonstration (TPD), is not subject to a similar criticism around the issue of self-selection. TPD was mandatory for first-time teenage mothers on welfare, who were required to participate in education, job training, or employment-related activities. Slightly less than 90 percent of the almost 6,000 teenage mothers who joined the welfare rolls in Camden and Newark, New Jersey, and Chicago, Illinois, between July 1987 and April 1990 were enrolled in the demonstration. Half the women were assigned to participate in the enhanced programs (experimental group), and half received regular AFDC services (control groups). Participants were surveyed at the beginning of their enrollment in AFDC. In addition, follow-up surveys were conducted two years and six years after intake. Response rates for both follow-ups exceeded 80 percent. (Unless otherwise noted, all data on the TPD program is from Kisker, Rangarajan, and Boller 1998.)

The average age of the participants was between 18 and 19 at all three sites. In Camden, about 56 percent of the participants were black, and 38 percent were Hispanic; 21 percent had completed high school or had a GED certificate. In Newark, about 71 percent were black, 15 percent were Hispanic, and 26 percent had completed high school or had a GED. In Chicago, 85 percent were black, 5 percent were Hispanic, and 40 percent had the equivalent of 12 years of schooling. Many of the participants who were in school were behind in grade level for their age. In Camden and Newark, more than 40 percent of the sample had reading skills below the sixth-grade level; in Chicago, the figure was about 30 percent.

The TPD program as mandatory involvement in education, training, or employment, with all three sites requiring 30 hours per week of participation in these activities. Although the sites developed on-site remedial education, GED, and job-readiness classes, they relied mainly on existing education, training, and employment services in their communities. Parents who consistently failed to participate in the activities were sanctioned. The sanctions consisted of reductions in the monthly AFDC grants of about $160 in New Jersey and $166 in Chicago.

Case-management services played a large role in the programs. Caseload sizes ranged from about 50 in New Jersey to about 100 in Chicago. Case managers helped the mothers develop education, training, and employment plans to move them toward self-sufficiency. In the year preceding the second follow-up survey, members of the experimental group averaged about 28 hours per week in any activity, 7 to 11 hours of schooling per week for those who were in an educational activity, and 15 to 19 hours per week for those in participating in a training activity.

During the initial assessment phase, participants were required to attend a series of workshops that covered motivation and employment preparation, life skills, parenting, family planning, personal grooming, health, and nutrition. The duration of the mandatory family-planning workshops varied widely across sites—from a total of 1.5 hours in Chicago to 54 hours in Newark. According to the evaluation report, “the Camden program offered a rich family planning workshop for all clients and case managers had smaller overall caseloads, permitting them to offer more intensive case management to all clients” (Kisker et al. 1998, 121) Nearly 85 percent of mothers participated in the Chicago workshop, 27 percent participated in the Camden workshop, and 21 percent participated in Newark.

The combination of such limited time devoted to family planning in Chicago and low participation in Camden and Newark suggests that TPD did not provide a sufficiently high level of family-planning services to reduce the rate of subsequent pregnancies among participants. The evidence bears out this presumption. On average, the mothers became pregnant twice during the six-year follow-up period—about 27 to 40 percent were pregnant within one year of intake, 59 to 71 percent became pregnant within three years, and 74 to 82 percent did so within five years. The average number of births ranged from 1.2 in Newark to 1.6 in Camden (see table 5). Only in Camden were there significant, though small, differences in the number of pregnancies and births between experimental and control group members—the women in the control group averaged 1.9 pregnancies, with 1.6 births, whereas the women in the experimental group averaged 1.7 pregnancies and 1.5 births. Since the evaluation report does not provide details about the family-planning workshops in Newark, Camden, and Chicago, it is not possible to judge whether program content could account for the differences across sites. In any event, these outcomes imply that the information about contraception and birth control provided by the workshops was not sufficient to reduce fertility. 

Home Visitation by Nurses
The final program type to be reviewed in this chapter is home visitation by nurses. These programs were designed to achieve a variety of infant and health-related goals, including reducing the incidence of extremely low birthweights, preterm deliveries, and fetal neurodevelopmental impairment. The nurses’ visits also were intended to prevent injuries to children resulting from abuse and neglect, to limit welfare dependence, to reduce compromised maternal life-course development (e.g., subsequent pregnancies and curtailed education and work opportunities), and to prevent the early onset of antisocial behavior in children. As detailed below, of all the programs reviewed in this chapter, home visitation by nurses is the only effort that showed consistently significant success at reducing subsequent births to participating welfare mothers.

It is therefore worthwhile to describe in some detail the overall philosophy that informs the design and implementation of this program. David Olds and his colleagues (1998), explain how theories of human ecology, self-efficacy, and human attachment have figured in their thinking:

human ecology theory emphasizes the importance of social contexts as influences on human development. Parents’ care of their infants, from this perspective, is influenced by characteristics of their families, social networks, neighborhoods, communities, and cultures, and interrelations among these structures. (p. 38) 

This outlook has important implications for the design of the program. In particular, services were provided in the clients’ home, so that the nurses could evaluate the family environment and enlist the participation of family members, friends, and the mothers’ partners in helping the women with their family planning and other activities.

In describing efficacy theory, Olds and his colleagues (1988) distinguish between outcome expectations, which are the “individual’s estimates that a given behavior will lead to a given outcome,” and efficacy expectations, which are the “individual’s beliefs that they can successfully carry out the behavior required to produce the outcome.” [p. 23] Efficacy theory implies that

because the power-of-efficacy information is greater if it is based on the individual’s personal accomplishments than if it derives from vicarious experiences and verbal persuasion, the home visitors emphasize methods of enhancing self-efficacy that rely on women actually carrying out parts of the desired behavior. . . . . [Furthermore], the visitors employ methods of behavioral and problem analysis that emphasize the establishment of realistic goals and behavioral objectives in which the chances for successful performance are increased. (p. 24) 

     Attachment theory posits that “human beings … have evolved a repertoire of behaviors that promote interaction between caregivers and their infants and that these behaviors tend to keep specific caregivers in proximity to defenseless youngsters thus promoting their survival, especially in emergencies” (p. 27).  Home-visitation programs extend this notion of attachment to the relationship between the visitor and the mother. In the case of the family-planning aspect of the program, this idea implies that the programs encourage visiting nurses to develop an empathic relationship with the mother and other family members.

     This more hands-on approach differs notably from the monetary incentives and case-management methods reviewed in this chapter. The intervention here is more intrusive, more directive, and more unequivocal in the value judgments being communicated. The authority of the health professional is invoked on behalf of the clearly stated end (among others) of avoiding a repeat pregnancy, the ultimate goal being to enhance the physical and mental well-being of both the mother and the newborn child. The evidence suggests that if one wants to have a measurable impact on fertility among welfare recipients, an approach embodying some of these features may be required. 

Program Design
The first home-visitation program was begun in 1977 in Elmira, a small, semirural community in upstate New York (Unless otherwise noted, all data on the home-visitation programs is from Olds et al. 1998. The program enrolled 400 women, 85 percent of whom were either low-income, unmarried, or teenaged. None had had a previous live birth, and 89 percent were white. Interviews and assessments were conducted at registration (before the 30th week of pregnancy), at the 34th, 36th, 46th, and 48th month; and at the 15th year of the children’s lives.

Children of families in the control groups received sensory and developmental screening at ages 12 months and 24 months. The children were then referred for further clinical evaluation and treatment, if necessary, and in some cases were provided with free transportation for well-child care through the child’s second birthday. There were two experimental groups; families in the first experimental group (“treatment 3” in the evaluation report) received these services and were assigned a nurse who visited them at home during the pregnancy. The second experimental group (“treatment 4”) received all these services, and the nurse continued to visit through the child’s second birthday. Nurses’ visits were scheduled once a week during the first month after enrollment and every other week until the birth of the baby. The nurses visited weekly for 6 weeks after the baby was born, twice a week until the 21st postnatal month, and once a month until the 24th postnatal month.

The nurse visitations were quite intensive. Each visit lasted about 90 minutes, and nurses were required to follow a detailed visit-by-visit program protocol that focused on personal health, environmental health, maternal role development, maternal life-course development, and family and friend support. One of the major postnatal objectives was to help the mothers use a reliable method of contraception. Each nurse had a caseload of 20 to 25 families and received regular clinical supervision.

The results of this intervention are encouraging. Among low-income, unmarried women, the rate of subsequent pregnancy was 42 percent lower for women in the experimental groups than for the control participants during the 4-year period after the delivery of the first child. At the 15-year follow-up interview, the experimental groups had had 1.1 births, compared with 1.6 subsequent births for the control group; the experimental groups had an average of 65 months between the births of their first and second children, compared with 37 months for the control group (see table 6). Again, this effect was observed among the subsample of mothers who had low incomes and were unmarried. (Recall that 85 percent of the sample were either low-income, unmarried, or teenaged.)

Beginning in 1990, a second trial of the home-visitation program was started in Memphis with a very different population of mothers. The program enrolled 1,139 women with no previous live births who had at least two of three risk factors—being unmarried, having less than 12 years of schooling, and being unemployed. In contrast to the Elmira study, 92 percent of the Memphis mothers were black, 97 percent were unmarried, and 85 percent came from poor households.

According to the interviews conducted at the 24th month of the first child’s life in the Memphis study, home visitations by nurses led to fewer subsequent pregnancies and live births. Specifically, women in the experimental group had 23-percent fewer second pregnancies and 32-percent fewer subsequent live births than did the women in the control group. However, statistically significant differences between the experimental and control groups were limited to women with high levels of psychological resources. Notice that this finding contrasts with the Elmira study, where the largest effects were for the least well-off people in the sample. 

Conclusions
Of course, no one can be certain about why the nurse home visits appear to have been more successful than other programs in reducing subsequent pregnancies. This uncertainty will not deter speculation, however. The home-visitation programs reviewed here differ from the financial-incentive and case-management efforts in three areas—the service provider, the population served, and the type of family-planning service offered. Let us consider these differences in more detail.

The service provider for the monetary-incentive and case-management programs generally was a caseworker, whose efforts were supplemented by professionals and paraprofessionals in charge of special aspects of the intervention. In some instances, the caseworkers received special training for the purposes of the experiment; often, however, they did not, or the training was insufficient to fully acquaint them with the program. The contrast with the home-visitation programs is notable: the service provider was a nurse explicitly trained in details of contraceptive practice, in techniques to help clients establish and achieve realistic goals, and in ways of enlisting the support of family members, friends, and the mothers’ partners.

Concerning the population served, home-visitation programs were voluntary, whereas some of the other programs were not. As our discussion of the New Chance demonstration indicated, voluntary interventions may attract a more selective population, which in turn may bias the measured treatment effect in either direction. The home-visitation programs included only women with no previous births, whereas most of the other programs enrolled only women with a previous birth. The Elmira home-visitation program served mainly white women in a semirural community, but participants in the other programs were much more likely to be black or Hispanic, live in large cities, and receive AFDC. The replication of the Elmira program in Memphis with a population more similar to the typical AFDC caseload is promising. The program effect in Memphis was smaller, however, and the subgroups benefiting most from the program differed between Elmira and Memphis.

            Consider now the difference between program types in the level and type of services provided. A sharp contrast can be drawn between home visitation and the other programs with respect to the usual point of service and amount of contact provided by the program. Nurses were sent to the home so that they could assess the environment where the client was living and enlist the support of others in the household to help the woman achieve the objectives set out in the program. In addition, the caseloads in the home-visitation programs were generally lower, and contact was much more frequent and regular.

Furthermore, family planning generally received more emphasis in the home-visitation programs, whereas education, training, and employment were often regarded as more important for many of the other experiments. The nurses’ training program and manual indicated that family planning was one of the topics to be covered regularly during visits with clients in the context of planning for the future. In particular, family planning in the home-visitation program arose in the context of a public health program designed to improve the mother and child’s physical, mental, and emotional health status. Nurses delivering these services had professional training in the use of contraceptives.

The professional ethos of nurses working in the home visitation field is quite different from that found among the social workers who typically serve as case managers in conventional pregnancy prevention programs.  As the director of a home visitation program in Dayton (not a part of the study cited above) told a reporter for the Washington Post: “We talk about using it [birth control] in foreplay . . . about leaving a space at the end of the condom. We give them colored condoms. I don’t know very many social workers who would be comfortable talking about that” (Vobejda 1998, A1). This speculation (about discomfort with such explicit talk) is certainly consistent with attitudes found among case managers in the New Chance program. Thus, it is likely that home-visitation programs provided more intensive information about family planning than other programs.

Evidence also shows that home-visitation programs provided a greater number of unambiguous, normative messages that becoming pregnant again is not desirable.  “The old strategy has been to say ‘If you want to avoid a second baby, here’s a condom and how to use it.’ The directive approach says, ‘You shouldn’t have another baby, and here are ways to prevent it’” (Vobejda 1998, A1). Because of the traditional role that nurses have played, they may be both more effective and more comfortable delivering such a normative message. In addition, because of their intensive and empathic interaction with the clients, the women may be more likely to hear and respond positively to authority of the nurse.

Thus, home visitation appears to be a promising approach deserving of further experimental study. Some uncertainty, however, remains as to what the sources of the differences in the experimental and control groups are. Evaluations of home-visitation programs that do not directly address pregnancy prevention reinforce this uncertainty. They indicate that the impact of such programs varies with the number and length of the home visits, the duration of the programs themselves (i.e., the typical times of initiation and termination), the content of the visits, the quality and nature of the visitor’s interaction with the family, the risk characteristics of the sample, and visitors’ level of training (Olds and Kitzman 1993).

Finally, there is a more general lesson to be learned from this comparative review of pregnancy-prevention efforts. The findings summarized here can be read as suggesting that economic incentives have only minimal leverage in this area of human behavior. This judgment, however, is premature. (After all, financial inducements were successful in raising participation rates in peer-group meetings in the Dollar-a-Day experiment in Denver. Moreover, there is plenty of evidence in the demography literature that fertility-related behaviors are broadly responsive to benefits and costs.) An alternative interpretation would emphasize the need for financial incentives to be coupled with some kind of directive intervention that tries to communicate a value-based message.

            Most economic analysis starts from the assumption that the preferences of people for alternative courses of action are givens and that behavior only can be changed by imposing rewards or punishments in an effort to alter each person’s cost-benefit calculations. An alternative approach makes it a principle objective of policy to alter peoples’ views about how they should live their lives. Many people are uncomfortable with this sort of thing—it smacks of paternalism and seems to usurp individual autonomy. Yet, given the maladies afflicting the clients of social service agencies throughout the land, such usurpation may be unavoidable. That is, a pedagogic function in public policy—showing citizens how to lead their lives better—may need to be invoked.

This conclusion is supported by the sharp contrast in the effectiveness of the family-cap and the nurse-visitation programs—a difference that seems clear, notwithstanding technical problems with the evaluations of the New Jersey and Arkansas experiments. Although this conclusion is advanced tentatively, it is sufficiently plausible that policy analysts should take it seriously and begin to consider how authoritative interventions can be most effectively and humanely designed. 

References
Besharov, D. J.; Germanis, P.; and Rossi, P. H. 1997. Evaluating welfare reform: A guide for scholars and practitioners. College Park: University of Maryland School of Public Affairs.

Camasso, M.; Harvey, C.; and Jagannathan, R. 1996. An interim report on the impact of New Jersey’s Family Development Program. New Brunswick, NJ: Rutgers University.

Camasso, M. J.; Harvey, C.; Jagannathan, R.; and Killingsworth, M. 1998a. A final report on the impact of New Jersey’s Family Development Program. New Brunswick, NJ: Rutgers University.

Camasso, M. J.; Harvey, C.; Jagannathan, R.; and Killingsworth, M. 1998b. A final report on the impact of New Jersey’s Family Development Program. Results from a pre-post analysis of AFDC case heads from 1990 to 1996. New Brunswick, NJ: Rutgers University.

Fairlie, R.W., and London, R. A. 1997. The effect of incremental benefit levels on births to AFDC recipients. Journal of Policy Analysis and Management 16(4):575–597.

Horvath, A., and Peters, H. E. 1999, September 16–17. Welfare waivers and non-marital childbearing. Paper presented at For Better and for Worse: State Welfare Reform and the Well-Being of Low-Income Families and Children. Washington, DC: Joint Center for Poverty Research.

Kisker, E. E.; Rangarajan, R.; and Boller, K. 1998. Moving into adulthood: Were the impacts of mandatory programs for welfare-dependent teenage parents sustained after the programs ended? Princeton, NJ: Mathematica Policy Research.

Martini, A., and Wiseman, M. 1997. Explaining the recent decline in welfare caseloads: Is the Council of Economic Advisers right? Washington, D.C.: The Urban Institute.

Olds, D. L.; Henderson, C. R.; Kitzman, H.; Eckenrode, J.; Cole, R.; Tatelbaum, R.; Robinson, J.; Petitt, L. M.; O’Brien, R.; and Hill, P. 1998.  Prenatal and Infancy Home Visitation by Nurses: A Program of Research. [unpublished draft research report, University of Colorado]

Olds, D., and Kitzman, H. 1993. Review of research on home visiting for pregnant women and parents of young children. Future Child, 3: 53-92.

Quint, J.C.; Bos, J. M.; and Polit, D. F. 1997. New Chance: Final report on a comprehensive program for young mothers in poverty and their children. New York, NY: Manpower Demonstration Research Corporation.

Steven-Simon, Dolgan, Kelly and Singer 1997. The effect of monetary incentives and peer support groups on repeat adolescent pregnancies. Journal of the American Medical Association, March 26, 1997, Vol. 277, pp. 977–982.

Turturro, C.; Benda, B.; and Turney, H. 1997. Arkansas Welfare Waiver Demonstration project: Final report. Little Rock: University of Arkansas.

Vobejda, B. 1998, May 13. Strictly speaking, success. The Washington Post. p. A1.

 

Table 1. Number of Births, Arkansas Welfare Waiver Demonstration

 

Experimental Group

Control Group

Mean

 0.16

 0.14

Standard deviation

(0.48)

(0.35)

 

Table 2. Post–Family-Cap Birth Rates—New Jersey Family Development Program

                                                                        Births (%)

Period

Experimental Group

Control Group

8/93–7/94

10.04

10.53

8/94–7/95

 5.64

 5.69

 

Table 3. Rate of Repeat Pregnancies—Dollar-a-Day Program 

 

Rate of Repeat Pregnancies (%)

 

Time Since Enrollment

 

 

Total

Meetings and Incentive

 

Meetings Only

 

Incentive Only

 

 

Control

 

6 months

 

 8.9

 

 7.2

 

 8.7

 

14.1

 

 4.6

 

12 months

 

19.8

 

18.6

 

30.4

 

22.6

 

11.1

 

18 months

 

29.0

 

27.8

 

34.8

 

34.5

 

18.2

 

24 months

 

39.0

 

35.1

 

56.5

 

41.7

 

34.1

 

Table 4. Pregnancy and Birth Rates—New Chance

Outcome

Experimental Group (%)

Control Group (%)

Pregnancy by month 42

75.2

72.8

Birth by month 42

54.7

55.3

  

Table 5. Number of Births 78 Months after Intake—Teenage Parent Demonstration

Location

Regular Services Group

Enhanced Services Group

Camden

1.6

1.5

Newark

1.2

1.2

Chicago

1.7

1.7

  

Table 6. Birth Rates and Timing—Elmira Home-Visitation Program

Outcome

Experimental Group

Control Group

Average number of births at 15-year follow-up

 

1.1

 

1.6

Average number of months between birth of first and second child

 

 

65

 

 

37

  



[1] An example of a hypothetical case was as follows: “An adolescent has a child while receiving AFDC assistance as part of her mother’s case which is already capped. The worker does not extend cash benefits to the adolescent’s child.” Less than half of the case managers surveyed realized that the cash grant should not have been capped. (See Camasso et al. 1996, pp. 139–145.)

[2] In theory, of course, selection bias can go in either direction. For example, an especially skilled population might respond more positively to some program treatment than would the welfare population at large.


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