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Chapter Seven
FAMILY STRUCTURE
7.1. BACKGROUND
As noted in Chapter 1, in addition to promoting work and reducing dependency, PRWORA aimed to reduce unwed childbearing, to promote marriage, and to maintain two-parent families. In this chapter, we turn to the impact of welfare reform on family structure, considering both marriage and childbearing.
PRWORA’s focus on reducing unwed childbearing, promoting marriage, and maintaining two-parent families was partially motivated by concern about trends in those outcomes. Up until about 1970, more than 85 percent of American children were being raised in two-parent families. Over the succeeding three decades, that figure fell to under 70 percent (see Figure 7.1) because of increases in nonmarital childbearing and, to a lesser extent, increases in divorce. Figure 7.2 shows that while in the 1950s less than 5 percent of births were to unmarried women, beginning in the early 1960s, this percentage began to increase sharply. By the early 1990s, one-third of births were to unmarried women. This rise in nonmarital childbearing was an important cause of the decrease in the share of children being raised by two parents.
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[D] |
As seen in both Figures 7.1 and 7.2, some of the trends in family structure and fertility appear to have slowed or stabilized in the latter part of the 1990s, about the time welfare reform was under way. Both the percentage of children living in two-parent families and the percentage of births to unmarried women has been approximately constant since 1994. The overall trend evident in Figure 7.1 is consistent with other recent analyses of family structure, with some evidence that the relative changes in one- versus two-parent families is more pronounced for families with lower income or less education, precisely the groups that are more likely to be affected by welfare reform (Acs and Nelson, 2001; Dupree and Primus, 2001).
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[D] |
In the case of fertility, the leveling-off of the trend for nonmarital childbearing seen in Figure 7.2 has been accompanied by a decline in teen fertility rates during the 1990s (Martin et al., 2001). For example, across all race and ethnic groups, the drop in teen fertility from 1991 to 2000 is 28.9 percent for 15—17-year-olds and 15.8 percent for 18—19-year-olds. Furthermore, the drop is particularly large for blacks (40.3 percent and 23.6 percent for 15—17-year-olds and 17—19-year-olds, respectively). However, some of the decline occurred in the early 1990s, before widespread welfare reform efforts, raising questions about the role that reform played in reducing teen fertility.
These trends are suggestive that welfare reform may have had some impact on fertility and family structure, and a number of provisions implemented by the states initially under section 1115 waivers and then TANF were designed to directly affect these outcomes. As noted in Chapter 2, a number of states instituted family caps with the objective of reducing additional childbearing for mothers already on welfare. Minor residency requirements are another feature designed to make unwed teen childbearing less attractive. In addition, by eliminating differences in eligibility for two-parent versus one-parent families (e.g., the "100-hour rule" and work history requirement), states aimed to diminish any disincentive toward marriage associated with welfare eligibility rules.55
PRWORA’s emphasis on family structure outcomes was partially motivated by an extension of the economic model of the effect of welfare programs developed in the earlier chapters. That extension views women as considering the structure of welfare programs when making choices not only about welfare and work, but also when making choices about family structure–whether to have children, whether to marry the father, and whether to subsequently divorce.
The theory’s implications follow from noting that welfare has primarily been paid to single mothers, but not to childless women, nor (under most circumstances) to married women.56 Welfare therefore lowers the price of raising a child when unmarried relative both to not having a child and relative to having a child and marrying (or not divorcing). Therefore, this model suggests that any policy change that makes welfare relatively more attractive (e.g., higher benefit levels or financial work incentives) will raise fertility (and especially nonmarital fertility) and decrease marriage. Conversely, any policy change that makes welfare relatively less attractive (e.g., a family cap, mandatory work-related activities, or time limits) will lower fertility (and nonmarital fertility) and increase marriage. However, when such reforms are enacted together, the combined effect on marriage and fertility is ambiguous.
These implications of economic theory assume that welfare is not available to married couples. However, welfare was potentially available to married couples under the AFDC Unemployed Parent (AFDC-UP) program and continues to be available under TANF. Making welfare payments to married couples increases the incentive to have children, but lowers the disincentive to marriage (Hu, 2000). As noted above, to further reduce the disincentives to be married, most states have reduced or eliminated the differential treatment of two-parent families under their TANF programs. For two reasons, however, the effects of the provisions of such welfare programs for married women are likely to be small. First, most married couples have income sufficiently high to make them income ineligible for welfare. Second, and perhaps as a consequence, the AFDC-UP program (under TANF, two-parent programs) are quite small in most states.
There are other mechanisms by which welfare reform may affect family structure. For example, if welfare-to-work programs succeed in raising earnings and income, they might make women more attractive spouses and, thus, raise the propensity to marry. At the same time, increased work may limit the time available for searching for a marital partner; then again, interactions at the workplace may ease marital search. As yet another example, low household income may increase the emotional and financial strain on a marriage, so that welfare reforms that raise total income might be expected to increase marriage and, in particular, to help those currently married to stay married.
Although welfare reform was motivated in part by trends in marriage and fertility, these outcomes are less well studied in both the experimental and econometric literatures. Of the random assignment studies we review in this report, WRP, IMPACT, TSMF, FIP, New Hope, SSP Plus, SSP Applicants, VIP/VIEW, PPI, and PIP do not analyze either marriage or fertility. CWPDP, MFIP, and SSP examine only marriage, while AWWDP and FDP consider only fertility. The remaining programs–L.A. Jobs-First GAIN, the 11 NEWWS programs, EMPOWER, ABC, FTP, and Jobs First–analyze both outcomes. Two econometric studies consider either marriage or living arrangements, while there are four econometric analyses of fertility.
Compared with the outcomes examined in Chapters 4, 5, and later in 8, the more limited research on marriage and fertility can be attributed to several factors. First, although PRWORA motivated reform in part by goals related to marriage and childbearing, many of the state programs evaluated under waivers were designed more to influence work and welfare use. Even so, a few of the programs that included family caps, minor residency requirements, and changes in two-parent eligibility requirements do not evaluate either marriage or fertility (e.g., IMPACT and VIP/VIEW).
Second, unlike welfare use, employment and earnings, and some measures of income, marriage and fertility behavior are harder to measure using administrative data (although this is the source of information on fertility for FDP and AWWDP). Thus, those demonstration studies that do not have participant surveys are less likely to consider these outcomes. Third, even when resources are devoted to measuring these outcomes, changes in marital status and additional childbearing while on welfare are relatively rare events and changes in behavior may not be immediate, whether for the recipient generation or for the next generation of daughters of the recipients. As a result, studies with short follow-up periods may be less likely to detect significant changes in these outcomes. In addition, survey data often have smaller samples and are subject to measurement error (e.g., recall bias and differential non-response), leading these analyses to have lower power.57 Consequently, these outcomes may not be included in impact analyses, and when they are, there may be limited statistical power to detect significant changes in behavior.
Fourth, the influence of welfare reform on marriage and fertility behavior is likely to affect women who are not on welfare just as much, if not more, than those who are on welfare. While welfare reform may affect the likelihood that a woman on welfare has additional children or gets married or stays married, it should also affect these decisions for women who are at risk of welfare participation. For these women, welfare reform may affect their likelihood of entering welfare. However, as noted in Chapter 3, conventional demonstration studies are not designed to capture welfare entry effects, so they will miss this pathway by which reforms may affect family structure. This is a significant limitation of the demonstration studies and stresses the need for high-quality econometric studies.
The remainder of this chapter proceeds by considering first the random assignment studies and then the econometric studies of family structure and its two primary components: marriage and fertility. Since there is only one demonstration study with subgroup analyses of marriage and fertility, we discuss these results along with the main results rather than in a separate section (or in Appendix A). After discussing the random assignment and econometric studies in turn, we proceed to a synthesis of the experimental and econometric evidence. The final section offers our conclusions.
7.2. RANDOM ASSIGNMENT STUDIES OF THE EFFECTS OF WELFARE REFORM ON FAMILY STRUCTURE
In this section, we consider the effects of random assignment studies on family structure, namely marriage, household size, and fertility. As noted above, most of the demonstration studies that consider these outcomes use survey data to assess whether a participant in the treatment or control group has had an additional child since random assignment or the participant’s marital status at the time of the follow-up survey. The follow-up interval ranges from 18 months to five years.
In assessing current marital status, studies differ in whether they differentiate between those who are married versus those who are married and living with their spouse. Some studies also report impacts for cohabitation, separate from being married, or combined with those who are married. A few studies also measure whether there was any change in marital status since random assignment, given that the respondent may have married and subsequently become separated, divorced, or widowed by the time of the follow-up. Finally, two studies measure household composition in terms of household size and the number of adults and children. Changes in household size may result from changes in marital status or additional childbearing, but also for other reasons such as "doubling up" with other relatives or nonrelatives, or departures of older children who move out of the household. Where possible, our discussion focuses on marriage with a spouse present, the concept that most closely aligns with PRWORA’s goals, but often only results for other outcomes (e.g., any cohabitation, marital or nonmarital) are available.
Fertility is typically measured for the survey respondent, and the measure is whether the respondent has had any children since random assignment. In one study, EMPOWER, childbearing while on welfare is measured both for case heads and unwed minors in the welfare case unit. That study and ABC also differentiate births since random assignment from conceptions since random assignment (defined as births more than 10 months since random assignment). For the other studies, some of the measured births may have been conceived prior to the time when the program rules becoming effective.
Finally, two studies use information from welfare data systems to measure children born to study participants. However, recording of births in welfare data systems is incomplete. Current welfare recipients have an incentive to report births. A reported birth will enable the child to be enrolled in Medicaid, and, in the absence of a family cap, the family’s welfare payment will increase. Births to mothers not receiving welfare are not recorded in any welfare data system. This is an important limitation because PRWORA’s interest in reducing out-of-wedlock childbearing is not limited to births among welfare recipients.
In the remainder of this section, we focus first on the results for marriage and household size, followed by the results for fertility. In both cases, we organize our discussion by the major reform or reforms considered by the demonstrations.
7.2.1 Marriage and Household SizeTable 7.1 records the results for the random assignment studies that examine marriage and household size. With the exception of Panel E, at least one study in each of the other policies or groups of policies in Panels A to F examines a measure of marriage.
Programs That Focus on Financial Work Incentives
As seen in Panel A of Table 7.1, results for two programs that focus on financial work incentives provide some evidence for an increase in marriage. Hu (2000) estimates the effects of the CWPDP on marital status. While he finds no effect for AFDC-Basic (i.e., single parent) cases, he finds that the experiment increased marriage for AFDC-UP cases. The effect appears to be the result of less divorce. The interpretation of these results is, however, complicated by policy bundling. The CWPDP waiver included a financial incentive; it also included a cut in the AFDC benefit level (at zero earnings) and removed some of the restrictions on eligibility of two-parent families (similar to those in MFIP discussed below). It is not clear which of the components of the bundle caused the marital status effect.
| Marital Status | Change in Marital Status | Household Size | ||||||||||||
|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|
| Name | Cases served | Data | Measure | Control mean | Impact | % | Measure | Control mean | Impact | % | Measure | Control mean | Impact | % |
| A. Programs that focus on financial work incentives | ||||||||||||||
| CWPDP | Single-parent recipients | S | R is married at 29-41 mo FU (%) | 13.7 | 2.1 | 15.3% | ||||||||
| Two-parent recipients | S | R is married at 29-41 mo FU (%) | 71.2 | 7.6** | 10.7% | |||||||||
| MFIP-IO | Urban single-parent recipients | S | R is married at the 36-mo FU (%) | 5.8 | 5.2** | 89.7% | ||||||||
| S | R is married or living with partner at the 36-moFU (%) | 20.8 | 2.7 | 13.0% | ||||||||||
| Urban single-parent applicants | S | R is married at the 36-mo FU (%) | 15.1 | -2.2 | -14.6% | |||||||||
| S | R is married or living with partner at the 36-moFU (%) | 29.6 | -2.6 | -8.8% | ||||||||||
| B. Programs that focus on financial work incentives tied to hours of work | ||||||||||||||
| SSP (a) | Single-parent recipients | S | R is married at 36-mo FU (%) | 9.5 | -0.6 | -6.3% | ||||||||
| S | R is married or in common law relationship at 36-mo FU (%) | 17.3 | 0.1 | 0.6% | R ever married or in common law relationship as of 36-mo FU (%) | 19.2 | 0.3 | 1.6% | ||||||
| C. Programs that focus on mandatory work-related activities | ||||||||||||||
| LA Jobs-1st GAIN | Single-parent recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 6.9 | 2.2 | 31.9% | ||||||||
| S | R is living with partner at 2-yr FU (%) | 8.5 | -1.1 | -12.9% | ||||||||||
| Atlanta LFA | Recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 4.0 | -0.3 | -7.5% | ||||||||
| S | R is married and living with spouse at 5-yr FU (%) | 8.4 | 1.3 | 15.5% | ||||||||||
| Grand Rapids LFA | Recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 11.8 | 1.3 | 11.0% | ||||||||
| S | R is married and living with spouse at 5-yr FU (%) | 20.5 | 2.3 | 11.2% | ||||||||||
| Riverside LFA | Recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 13.4 | -2.7* | -20.1% | ||||||||
| S | R is married and living with spouse at 5-yr FU (%) | 22.0 | -1.4 | -6.4% | ||||||||||
| Portland | Recipients and applicants; no cases with substantial barriers | S | R is married and living with spouse at 2-yr FU (%) | 9.0 | -0.2 | -2.2% | ||||||||
| S | R is married and living with spouse at 5-yr FU (%) | 23.6 | -6.2 | -26.3% | ||||||||||
| Atlanta HCD | Recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 4.0 | -1.2 | -30.0% | ||||||||
| S | R is married and living with spouse at 5-yr FU (%) | 8.4 | -1.5 | -17.9% | ||||||||||
| Grand Rapids HCD | Recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 11.8 | 0.3 | 2.5% | ||||||||
| S | R is married and living with spouse at 5-yr FU (%) | 20.5 | -0.2 | -1.0% | ||||||||||
| Riverside HCD | Recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 10.9 | 1.6 | 14.7% | ||||||||
| S | R is married and living with spouse at 5-yr FU (%) | 18.1 | 3.7 | 20.4% | ||||||||||
| Columbus Integrated | Recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 9.0 | 1.1 | 12.2% | ||||||||
| Columbus Traditional | Recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 9.0 | 0.9 | 10.0% | ||||||||
| Detroit | Recipients and applicants | S | R is married and living with spouse at 2-yr FU (%) | 7.6 | -3.4 | -44.7% | ||||||||
| Oklahoma City | Applicants | S | R is married and living with spouse at 2-yr FU (%) | 19.1 | -3.4 | -17.8% | ||||||||
| D. Programs that focus on financial work incentives and mandatory work-related activities | ||||||||||||||
| MFIP | Urban single-parent recipients | S | R is married at the 36-mo FU (%) | 5.8 | 2.8 | 48.3% | ||||||||
| S | R is married or living with partner at the 36-mo FU (%) | 20.8 | 3.2 | 15.4% | ||||||||||
| Urban single-parent applicants | S | R is married at the 36-mo FU (%) | 15.1 | 1.7 | 11.3% | |||||||||
| S | R is married or living with partner at the 36-mo FU (%) | 29.6 | 4.1 | 13.9% | ||||||||||
| E. Programs that focus on other individual reforms | ||||||||||||||
| F. Programs that focus on TANF-like bundle of reforms (time limits with financial incentives, work-related activities, or both) | ||||||||||||||
| EMPOWER (b) | Recipients | S | R is married at 3-yr FU(%) | 28.9 | -0.9 | -3.1% | R changed marital status since RA as of 3-yr FU (%) | 7.7 | 0.0 | 0.0% | ||||
| ABC | Single parent recipients and applicants | S | R is married and living with spouse at 4-19-mo FU (%) | 7.6 | 1.4* | 18.4% | ||||||||
| FTP | Recipients and applicants | S | R is married and living with spouse at 4-yr FU (%) | 19.1 | -1.9 | -9.9% | Total number of HH members (including R) at 18-mo FU | 3.9 | 0.0 | 0.0% | ||||
| Jobs First | Recipients and applicants | S | R is married and living with spouse at 18-mo FU (%) | 7.0 | -1.2 | -17.1% | R changed marital status since RA as of 18-mo FU (%) | 19.9 | -1.7 | -8.5% | Total number of HH members at 18-mo FU | 3.3 | 0.2*** | 7.6% |
| S | R is married and living with spouse at 3-yr FU (%) | 10.8 | -1.6 | -14.8% | Total number of HH members at 3-yr FU | 3.4 | 0.1 | 2.9% | ||||||
| NOTES: For full program names and citations,
see Table 3.4. Abbreviations: A=administrative data; S=survey data;
FU=follow-up; HH=household; R=respondent; RA=random assignment. * = statistically significant at the 10 percent level; ** = statistically significant at the 5 percent level; *** = statistically significant at the 1 percent level. (a) New Brunswick and British Columbia combined. (b) Phoenix site only, cash assistance. |
MFIP-IO is a pure financial incentive program, and its financial work incentives were deliberately designed to encourage marriage. Some restrictions on eligibility for two-parent families were eliminated, and the treatment of stepparent earnings was liberalized. Consistent with this intention, the experimental evaluation of the financial work incentives alone (i.e., MFIP-IO) suggests that marriage increases. For single parent recipients, the fraction married at the time of the 36-month follow-up interview is 11.0 percent in the treatment group versus 5.8 percent in the control group, a statistically significant difference of 5.2 percent. The impact is also positive on the combined status of married or cohabiting, but the difference is not significant. For single parent applicants, treatment group members are less likely to be married–or married or cohabiting–but again the difference is not significant.
Programs That Focus on Financial Work Incentives Tied to Hours of Work
Among the programs that tied financial work incentives to hours of work, SSP is the only one that assesses the impact on marriage behavior (Panel B of Table 7.1). The structure of SSP’s incentives was specifically designed to lower disincentives to marry. Canada’s Income Assistance program counts a husband’s income when calculating the welfare benefit. If the husband works, this will usually result in a lower benefit and thus would be expected to discourage marriage. In contrast, SSP disregards income contributed by a husband or common-law spouse when calculating the earnings supplement, thereby removing the disincentive and encouraging marriage. However, the higher household income under SSP (discussed further in Chapter 8) might have been expected to induce some women to choose to live on their own, thus decreasing marriage.
SSP includes a measure of marital status as well as a broader measure that includes both formal marriage and Canadian common-law relationships.58 Using this combined marriage and common-law relationship concept, SSP has insignificant impacts. Marriage is slightly less common; common-law relationships are slightly more common; neither effect is statistically different from zero.
The interpretation of the SSP results is, however, complicated by considering the two provinces–British Columbia and New Brunswick–separately. For almost all outcomes considered in the SSP evaluation, impacts do not differ significantly across the two provinces. Marriage is the exception. Using the broad SSP definition, marriage significantly decreases in British Columbia (by 3.1 percentage points, or 18 percent of the value for the control group); while marriage significantly increases in New Brunswick (by 4.1 percentage points; or 20 percent). Using a narrow definition of marriage that excludes common law relationships, the effect in British Columbia is still negative, but at p < 0.10 (but not at p < 0.05). The effect in New Brunswick is still positive, but not statistically different from zero. The difference is significant at p < 0.10, but not at p < 0.05.
Michalopoulos et al. (2000) discuss the possible reasons for the difference in results across provinces. They note that the results within each province are robust across subgroups, so that the small differences in baseline characteristics between the two provinces do not explain the differences in impact. They also note that the impacts on income and full-time employment were similar across the two provinces and the policy changes removing the marriage penalty were identical.
They suggest two other plausible reasons for the divergence across provinces. A first reason relates to the marriage market. During the period of the experiment, the unemployment rate for men was considerably higher in New Brunswick than in British Columbia. They speculate that these poor job prospects for men made the additional employment, earnings, and income provided by SSP more attractive. It should be noted that this argument–that poor economic prospects for men encourage them to marry–is the opposite of the standard argument that marriage among American black women is low because there are few marriageable men (Wilson and Neckerman, 1987). A second reason concerns cultural differences. New Brunswick is more rural, and the majority is Catholic; British Columbia is more urban, and there are fewer Catholics. With only two sites and nominally identical programs, more definite conclusions are not possible. They conclude: "The opposite direction of impacts by province underscores the importance of geographic and cultural context in translating employment and earnings impacts into effects on family structure."
Programs That Focus on Mandatory Work-Related Activities
With one exception, the programs that evaluate mandatory work-related activities show no significant impacts on the fraction married and living with their spouse as of the two-year follow-up survey. As seen in Panel C of Table 7.1, the 12 insignificant impacts are evenly divided in sign and most involve a small percentage point change. Only Riverside LFA has a marginally (p < 0.10) statistically significant negative impact on the likelihood of being married. For seven of the NEWSS sites, there are also five-year follow-up results. In none of them (including Riverside LFA) can we reject the hypothesis of no effect. Again, the sites are divided in sign and the point estimates are small.
Programs That Focus on Financial Work Incentives and Mandatory Work-Related Activities
Among programs that combine financial work incentives with mandatory work-related activities, only MFIP assesses the impact on marriage defined as marriage alone and a broader measure that includes cohabitation (see Panel D of Table 7.1). For both urban single parent recipients and applicants, the MFIP impacts on the narrow (marriage) and broad (cohabitation) measures are positive, but none are statistically significant.59
In addition, the MFIP evaluation considered the impact of the full program on marriage for the sample of two-parent families (results not shown). For that study sample, the MFIP intervention increased the fraction remaining married by nearly 40 percent, from 48.3 percent for the control group to 67.4 percent for the treatment group, and the result is statistically significant. Analyses of other outcomes suggest that the effect is concentrated among those married (rather than cohabiting) at random assignment and works partially through a drop in the divorce rate (about 6.5 percentage points). The balance of the effect appears to be higher rates of married couples living together. Furthermore, these results are confirmed and strengthened by an analysis of official divorce records. Five years post-randomization, the control group had a 20 percent divorce rate, while the experimental families had an 11 percent divorce rate.
Finally, we note that these results are consistent with the MFIP-IO results that also find an effect on marriage. Since the studies of mandatory work-related activities alone find no effect on marriage, it seems reasonable to interpret the main MFIP results (including mandatory work-related activities) as a financial incentive effect, lending more support to the inference that financial work incentives increase marriage.
Programs That Focus on TANF-Like Bundles of Reforms
Finally, four of the programs that involve TANF-like bundles of reforms assess marriage and, in two cases each, changes in marital status (EMPOWER and Jobs First) and household size (FTP and Jobs First). The follow-up periods range from as little as four months (ABC, for those entering latest) to four years (FTP). EMPOWER, FTP, and Jobs First have negative but insignificant impacts on the likelihood of being married (or married and living with their spouse). Changes in marital status in EMPOWER and Jobs First and are also insignificant. The impact on household size is zero for FTP but small, positive, and significant for Jobs First, where household size increases by 0.2 persons. Disaggregation by adults and children (not shown) shows the increase is evenly split between the two types of household members.
ABC is the only study to show a statistically significant (p < 0.10) increase in marriage, and this occurs even though the follow-up period averages 12 months, with a range from 4 to 19 months. Analyses for subgroups show a significant positive impact on marriage for women under 25, those who are capable of having additional children, those never married, and those with less than 12 years of schooling. The differences between age and education groups are also statistically significant. There are no significant impacts for subgroups defined by length of prior welfare receipt. A broader measure that includes living with a spouse or the respondent expects to marry shows no significant impact overall. For this broader measure of marriage and marriage expectations, the only significant difference for subgroups is by education, again with the least educated having the largest impact.
7.2.2. Fertility
Like marriage, with a few exceptions, the results for births since random assignment summarized in Table 7.2 are small and insignificant. For this outcome, results are available only for programs that focus on mandatory work-related activities, on family caps, and on TANF-like bundles of reforms.
Programs That Focus on Mandatory Work-Related Activities
Of the 12 studies that focus on mandatory work-related activities, only Columbus Traditional has a borderline statistically significant negative impact on births in the two years following random assignment. Against the prediction of the theory, the signs of the impacts in the other sites are more often positive than negative. For seven of the sites (but not Columbus), there are also five-year follow-up results. For none of these sites can we reject the hypothesis of no effect. Again, the signs are mixed, with more positive point estimates than negative point estimates.
| Fertility | ||||||
|---|---|---|---|---|---|---|
| Name | Cases served | Data | Measure | Control mean | Impact | % |
| A. Programs that focus on financial work incentives | ||||||
| B. Programs that focus on financial work incentives tied to hours of work | ||||||
| C. Programs that focus on mandatory work-related activities | ||||||
| LA Jobs-1st GAIN | Single-parent recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 9.3 | -0.2 | -2.2% |
| Atlanta LFA | Recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 6.4 | 0.5 | 7.8% |
| S | R had new baby present in HH as of 5-yr FU (%) | 12.4 | -0.8 | -6.5% | ||
| Grand Rapids LFA | Recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 11.1 | 1.9 | 17.1% |
| S | R had new baby present in HH as of 5-yr FU (%) | 21.7 | 0.9 | 4.1% | ||
| Riverside LFA | Recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 12.7 | -0.2 | -1.6% |
| S | R had new baby present in HH as of 5-yr FU (%) | 22.1 | 3.4 | 15.4% | ||
| Portland | Recipients and applicants; no cases with substantial barriers | S | R had child since RA as of 2-yr FU (%) | 10.7 | -1.2 | -11.2% |
| S | R had new baby present in HH as of 5-yr FU (%) | 22.7 | -5.3 | -23.3% | ||
| Atlanta HCD | Recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 6.4 | 1.4 | 21.9% |
| S | R had new baby present in HH as of 5-yr FU (%) | 12.4 | 0.1 | 0.8% | ||
| Grand Rapids HCD | Recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 11.1 | 2.4 | 21.6% |
| S | R had new baby present in HH as of 5-yr FU (%) | 21.7 | 0.5 | 2.3% | ||
| Riverside HCD | Recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 13.6 | 0.7 | 5.1% |
| S | R had new baby present in HH as of 5-yr FU (%) | 23.1 | 1.0 | 4.3% | ||
| Columbus Integrated | Recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 7.9 | 1.7 | 21.5% |
| Columbus Traditional | Recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 7.9 | -3.2* | -40.5% |
| Detroit | Recipients and applicants | S | R had child since RA as of 2-yr FU (%) | 12.3 | -2.6 | -21.1% |
| Oklahoma City | Applicants | S | R had child since RA as of 2-yr FU (%) | 14.9 | 0.7 | 4.7% |
| D. Programs that focus on financial work incentives and mandatory work-related activities | ||||||
| E. Programs that focus on other individual reforms | ||||||
| AWWDP | Recipients and applicants | A | Avg. number of births since RA as of 5-yr FU | 0.16 | 0.0 | -12.5% |
| FDP | Recipients | A | Regression-projected likelihood of R having a child since RA as of 17-Q FU (%) | 34.9 | -3.2** | -9.2% |
| Applicants | A | Regression-projected likelihood of R having a child since RA as of 17-Q FU (%) | 30.3 | -3.7** | -12.2% | |
| F. Programs that focus on TANF-like bundle of reforms (time limits with financial incentives, work-related activities, or both) | ||||||
| EMPOWER (a) | Recipients | S | Case head had child since RA as of 3-yr FU (%) | 18.0 | -1.0 | -5.6% |
| S | Case head conceived a child since RA as of 3-yr FU (%) | 11.3 | 0.1 | 0.9% | ||
| S | Unwed minor had child since RA as of 3-yr FU (%) | 4.0 | -2.4** | -60.0% | ||
| S | Unwed minor conceived a child since RA as of 3-yr FU (%) | 2.9 | -1.8* | -62.1% | ||
| ABC | Single parent recipients and applicants | S | R conceived a child since RA as of 4-19-mo FU (%) | 13.8 | -0.3 | -2.2% |
| FTP | Recipients and applicants | S | R had child since RA as of 4-yr FU (%) | 22.7 | 1.2 | 5.3% |
| Jobs First | Recipients and applicants | S | R had child since RA as of 18-mo FU (%) | 24.3 | -0.2 | -0.8% |
| S | R had child since RA as of 3-yr FU (%) | 20.7 | 0.1 | 0.5% | ||
| NOTES: For full program names and citations, see
Table 3.4. Abbreviations: A=administrative data; S=survey data; FU=follow-up;
HH=household; R=respondent; RA=random assignment. * = statistically significant at the 10 percent level; ** = statistically significant at the 5 percent level; *** = statistically significant at the 1 percent level. (a) Phoenix site only, cash assistance. |
Programs That Focus on Family Caps
Two experiments, FDP and AWWDP, evaluated a family cap. Both studies rely on administrative data from the welfare system to identify births after random assignment. They therefore analyze only the effect of the experiment on births while on welfare. This is a different concept from that analyzed by the other studies of fertility effects.
Like the results for other outcomes (e.g., welfare use and earnings), the evaluation of the AWWDP in Arkansas finds no effect on fertility. In addition, there was no statistically significant effect on participation in family planning or use of birth control. However, several methodological issues suggest caution in interpreting these findings. First, the sample size used for the analysis of fertility is very small: the researchers use a 5 percent random subsample of the population available for study. Thus, for their analysis of births, the samples sizes in the treatment and control groups are 86 and 88, respectively. Such small samples make it difficult to detect even moderate sized effects.
Second, the AWWDP evaluators report that "a substantial portion of workers explained the cap on benefits to clients in both the experimental and control groups" (Turturro, Benda, and Turney, 1997, p. 2). It is therefore not surprising that the family cap appears to have been only poorly understood. In a small survey of study participants (N = 102), about half did not know how their benefits would change with an additional child (45.7 in the experimental group versus 51.8 percent in the control group). Inasmuch as members of the control group believed that they were subject to the family cap, the experiment will underestimate its true effect.
Results for New Jersey are quite different. In New Jersey, the family cap was instituted as part of FDP, a wide-ranging waiver package including enhanced welfare-to-work services, financial work incentives, transitional Medicaid, and elimination of some marriage penalties. Comparisons of the experimental and control groups imply that for recipients the entire package of reforms led to a statistically significant decline in fertility of 9 percent, but there was no effect on abortion (not shown). For applicants, FDP resulted in a statistically significant 12 percent decline in fertility. In addition, abortions increased 14 percent, but this effect appears to be concentrated in the early months of the experiment, with convergence by the end of the analysis period (1996, four years later).
The experimental analysis of FDP also found effects on family planning. Survey questions indicate that, compared to those in the control group, those in the treatment group were 4 percentage points more likely to use family planning in the last year (30.9 percent versus 26.6 percent). Regression analyses of sterilization and family planning visits from Medicaid files are also consistent with a moderate to large effect on fertility practices, and the timing of these effects is also plausible.
Like AWWDP, however, methodological issues suggest concern in interpreting the findings. First, randomization does not appear to have been performed properly. More than one-quarter of case workers admitted to evaluators that they used discretion when making assignments to the treatment and control groups (Camasso et al., 1996). Second, like the Arkansas demonstration, the FDP client survey suggests that understanding of the program was very poor.60 Combining the groups that reported either that their cash benefits would not increase or that none of their benefits (including food stamps and Medicaid) would increase, survey results suggest that only 3.5 percent more of the experimental group believed that the cash benefit would not increase with the birth of a new child.
If understanding of the program was truly this weak, then the large fertility and abortion effects that were found are surprising. Poor recipient understanding of the family cap would be expected to bias the effects of the program downward relative to more complete understanding. These results would then imply even larger effects when the program was understood. Another interpretation is possible. FDP was broader than the family cap. It also involved an enhanced earnings disregard, enhanced case management, and relaxation of the marriage penalty. Thus, even if recipients did not understand the family cap, fertility effects might have resulted from these other program components.
Nevertheless, less than perfect understanding by the treatment and control groups of the policies that applied to them would still lead to a downward bias in the estimated program impact. Partially to address this concern, the New Jersey evaluation also conducted a before-and-after econometric analysis. In particular, again using the administrative data, Camasso et al. (1999) estimated a standard regression model for fertility with controls for demographic characteristics (e.g., age, marital status, education, and number of children), earnings, history of AFDC use, the unemployment rate, the FDP participation rate, county dummies, and a linear time trend. The effect of FDP was estimated as the deviation from the time trend implied by this regression model. Again, large negative effects of FDP on fertility were detected, as were moderate positive effects on abortions. Note, however, that by our standards for judging observational studies, this is a weak design. If fertility began to decline (or the decline accelerated) nationally for welfare recipients (as Figure 7.1 suggests), this approach would have attributed that decline to FDP. A stronger design would have included some form of control for trends in other states (which did not implement a family cap); however, as a New Jersey-specific evaluation, the evaluators did not have easy access to such data.
Programs That Focus on TANF-Like Bundles of Reforms
The four programs that focus on TANF-like bundles of reforms all find small and insignificant impacts on births or conceptions for the recipient for a follow-up interval ranging from four months (ABC) to four years (FTP). Three of the six impact estimates are negative. ABC also included an analysis of fertility desires (results not shown) by asking whether the respondent wants to have more children. Overall the impact estimate is negative but insignificant. Subgroup analyses for ABC showed a significant reduction in conceptions only for those on welfare between one and two years in the past five years. There was also a significant negative impact on fertility desires for this subgroup. In addition, the impact on fertility desires was significantly negative for women age 25 and above and for those ever married.
EMPOWER also measures births and conceptions for unwed minors and finds statistically significant negative impacts for both measures. As seen in Table 3.5, EMPOWER’s reforms included a family cap, as well as a minor residency requirement and a provision removing the exemption from JOBS participation for teens under age 16 (those age 13 and above must now participate). Because these three reforms are bundled with the program’s other reforms; it is not possible to ascribe the reduction in unwed teen fertility to these specific policies. It is also worth noting that the control group in EMPOWER became subject to the treatment group provisions two years into the three-year follow-up period. Thus, some of the measured impact of the EMPOWER reforms on adult and teen fertility may have been diluted by the control-group crossover.
7.3. ECONOMETRIC ANALYSES OF THE EFFECTS OF WELFARE REFORM ON FAMILY STRUCTURE
The effects of waivers and TANF on family structure have also been explored using econometric methods. As noted earlier, since welfare reform’s effect on family structure may be expected to operate primarily through entry effects that are not captured by random assignment studies, econometric approaches are likely to be more appropriate.
Table 7.3 summarizes the results of the two econometric studies that consider marriage and living arrangements using CPS data, and all but one of the studies considering fertility and abortion. Table 7.4 provides additional results from another study of a fertility outcome–the nonmarital fertility ratio. We begin by discussing results for marriage and living arrangements, followed by those for fertility.
7.3.1. Marriage and Living Arrangements
Schoeni and Blank (2000) consider the propensity to be married and the propensity to be a female head of household using the March CPS. (See the discussion of their analyses of other outcomes in earlier chapters.) As seen in Section A of Table 7.3, their DoD specification suggests that for high school dropouts, any implemented waiver increases marriage (by about 2 percentage points) and depresses female headship (also by about 2 percentage points). For those with exactly 12 years of schooling, waivers have a significant negative effect on marriage (not what would be expected) and a positive (but not statistically significant) effect on female headship. For those with more than 12 years of schooling, waivers again have a significant positive effect on marriage, but not female headship.
| Other controls | |||||||||||||
|---|---|---|---|---|---|---|---|---|---|---|---|---|---|
| Study | Data | Sample population | Begin | End | Outcome | Dep. var. | Policy var. | Coeff. (s.e.) | % effect | Economy | Demogr. and Geogr. | Fixed Effects | Policy |
| A. Marriage and Headship | |||||||||||||
| Schoeni and Blank (2000) | CPS aggregated | women 16-54, educ<12 | 76 | 98 | Percent married | Level | Any waiver | 0.0229 (0.0073) | 5.4 | U, U-1, EG, each *E |
A, E, A*E, R | S, Y, state time trends, Y*E |
B, B*E |
| women 16-54, educ=12 | Any waiver | -0.0144 (0.0060) | -2.2 | ||||||||||
| women 16-54, educ>12 | Any waiver | 0.0075 (0.0049) | 1.3 | ||||||||||
| women 16-54, educ<12 | TANF | -0.0004 (0.0171) | -0.1 | ||||||||||
| women 16-54, educ=12 | TANF | -0.0161 (0.0150) | -2.5 | ||||||||||
| women 16-54, educ>12 | TANF | 0.0034 (0.0114) | 0.6 | ||||||||||
| Schoeni and Blank (2000) | CPS aggregated | women 16-54, educ<12 | 76 | 98 | Percent head of household | Level | Any waiver | -0.0171 (0.0070) | -8.2 | U, U-1, EG, each *E |
A, E, A*E, R | S, Y, state time trends, Y*E |
B, B*E |
| women 16-54, educ=12 | Any waiver | 0.0052 (0.0058) | 2.3 | ||||||||||
| women 16-54, educ>12 | Any waiver | -0.0014 (0.0047) | -0.5 | ||||||||||
| women 16-54, educ<12 | TANF | -0.0133 (0.0165) | -6.4 | ||||||||||
| women 16-54, educ=12 | TANF | -0.0025 (0.0144) | -1.1 | ||||||||||
| women 16-54, educ>12 | TANF | 0.0239 (0.0110) | 8.5 | ||||||||||
| B. Living Arrangements | |||||||||||||
| Bitler, Gelbach and Hoynes (2001) | CPS micro data | women 16-54 | 84 | 98 | Number of persons in household | Level | Any waiver | 0.055 (0.020) | 1.2 | U, U-1, EG |
R, MSA, CC | S, Y | B |
| TANF and ever had waiver | 0.100 (0.037) | 2.2 | |||||||||||
| TANF and never had waiver | 0.042 (0.038) | 0.9 | |||||||||||
| Bitler, Gelbach and Hoynes (2001) | CPS micro data | women 16-54 | 84 | 98 | Number of children in household | Level | Any waiver | 0.030 (0.017) | 1.3 | U, U-1, EG |
R, MSA, CC | S, Y | B |
| TANF and ever had waiver | 0.065 (0.028) | 2.8 | |||||||||||
| TANF and never had waiver | 0.025 (0.027) | 1.1 | |||||||||||
| Bitler, Gelbach and Hoynes (2001) | CPS micro data | women 16-54 | 84 | 98 | Number of families in household | Level | Any waiver | 0.018 (0.007) | 1.6 | U, U-1, EG |
R, MSA, CC | S, Y | B |
| TANF and ever had waiver | 0.023 (0.011) | 2.0 | |||||||||||
| TANF and never had waiver | 0.026 (0.011) | 2.2 | |||||||||||
| C. Fertility | |||||||||||||
| Levine (2001) | State-level vital statistics | women 15-44 | 85 | 96 | Birth rate | Log | Any waiver | -0.030 (0.007) | -3.0 | U | R, A, E, MS | S, Y, ST |
B, PI, MD |
| Family cap | 0.050 (0.010) | 5.0 | |||||||||||
| Kearny (2001) | State-level vital statistics | women 15-34 | 89 | 98 | Number of births | Log | Any waiver | 0.003 (0.003) | 0.3 | U | A | S, Y, ST |
B, WE |
| TANF | 0.007 (0.005) | 0.7 | |||||||||||
| Family cap | 0.001 (0.004) | 0.1 | |||||||||||
| Time limit | -0.002 (0.003) | -0.2 | |||||||||||
| Kaushal and Kaestner (2001) | CPS micro data | unmarried women 18-44 with high school or less | 95 | 99 | Had a birth in last year | quasi-DoDoD w/married women high school or less | Low Intensity Reforms (waiver or TANF) | -0.010 (0.005) | -24.4 | U, U-1, U-2 |
A, R, N<6, N>=6, UI | S, Y | |
| Medium Intensity Reforms (waiver or TANF) | -0.001 (0.005) | -2.4 | |||||||||||
| High Intensity Reforms (waiver or TANF) | 0.020 (0.009) | 48.8 | |||||||||||
| Family cap | 0.009 (0.006) | 22.0 | |||||||||||
| Time limit | 0.003 (0.006) | 7.3 | |||||||||||
| Kaushal and Kaestner (2001) | CPS micro data | unmarried mother with high school or less | 95 | 99 | Had a birth in last year | quasi-DoDoD w/married mothers high school or less | Low Intensity Reforms (waiver or TANF) | 0.001 (0.007) | 1.8 | U, U-1, U-2 |
A, R, N<6, N>=6, UI | S, Y | |
| Medium Intensity Reforms (waiver or TANF) | 0.009 (0.007) | 15.8 | |||||||||||
| High Intensity Reforms (waiver or TANF) | 0.027 (0.013) | 47.4 | |||||||||||
| Family cap | 0.011 (0.008) | 19.3 | |||||||||||
| Time limit | 0.013 (0.008) | 22.8 | |||||||||||
| D. Abortion | |||||||||||||
| Levine (2001) | AGI survey | women 15-44 | 85 | 96 | Abortion rate | Log | Any waiver | -0.022 (0.031) | -2.2 | U | R, A, E, MS | S, Y, ST |
B, PI, MD |
| Family cap | 0.086 (0.063) | 8.6 | |||||||||||
| NOTES: Abbreviations: s.e. = standard error; U=unemployment rate; U-1=lagged unemployment rate; U-2=twice lagged unemployment rate; EG=employment growth; A=age, E=education, R=race, MS=marital status; N<6=Number of children less than 6; N>=6=Number of children 6 or older; UI-Unearned Income; MSA=Metropolitan Statistical Area (urban), CC=Central city; B=maximum welfare benefit; PI=Parental involvement in abortion to minors; MD=Mandatory delay in abortion; WE=Work exemption; S=state; Y=year; ST=state trends. |
They also estimate the effect of TANF using interstate variation in the date of implementation of each state’s TANF program. These models show almost no significant effect of TANF on marriage or female headship. The only exception is a 2 percentage-point increase in female headship for those with more than a high school diploma (not shown in the tables). There is also a small (less than 1 percent), but statistically insignificant, increase in marriage, although in alternative specifications there is a small, but statistically significant (at the 10 percent level), negative effect on marriage (the opposite of the expected sign).
Bitler, Gelbach, and Hoynes (2001) use the March CPS to explore the effect of welfare reform on living arrangements (Panel B of Table 7.3). In addition to the possibility that welfare reform might increase marriage, they hypothesize that welfare reform might also increase "doubling up" (i.e., moving in with other relatives, such as an aunt or grandmother of the children). Consistent with their hypothesis, they find evidence that welfare waivers increase several measures of doubling up: The number of persons in the household (at the 5 percent level), the number of children (only at 10 percent level), the number of families, the number of females, the number of males (only at the 10 percent level), and the number of "families" with kids (p < 0.05).
Related research (not shown in Table 7.3) also contributes to our understanding of the potential impact of welfare reform on marriage. Rosenbaum (2000) takes a more structural approach to the effect of government policies–including waivers, but primarily the EITC–on marriage (similar to that of Meyer and Rosenbaum, 2000, on employment). Using both the CPS and the SIPP, he finds strong effects of financial work incentives on marriage. A $1,000 marriage penalty from a combination of welfare and taxes (including the EITC) decreases the fraction of women married by about 5 percentage points, and the effects appear to be concentrated in entries into marriage, not exits from marriage. He also considers three explicit reform measures–(1) any waiver application, (2) a broadly defined time limit combining what we refer to as "time limits" (leading to a decrease in or termination of the welfare benefit) and what we refer to as "work triggers" (leading to a requirement for work or participation in a welfare-to-work activity), and (3) a binding time limit (i.e., benefits have been cut because at least some recipients have reached what we refer to as a "time limit"). Only one of the waiver proxies significantly affects marriage rates, and only in the CPS specification (not the SIPP specification). Moreover, the estimated effect is contrary to expectation: A time limit is estimated to lower marriage rates. Similarly, in the SIPP models of entry to and exit from welfare, a time limit counterintuitively lowers the probability of entry into marriage. Rosenbaum notes that these results appear to be quite sensitive to the details of the specification, suggesting caution in using these results for policy.
Ellwood (2000) uses CPS data from 1986 to 1998 (mostly the waiver period) to explore the effect of public policy on marriage. He parameterizes states by the "aggressive[ness] of welfare reform policies" but finds no effect of either the EITC or welfare policy on marital status.
Finally, two studies have explored the effect of child support enforcement on marital status. The theoretically expected effect is ambiguous. Better child support enforcement makes divorce more attractive for mothers, but less attractive for fathers. The interactions with the welfare system are complicated. Under the baseline AFDC rules, mothers kept only the first $50 of child support paid and the possibility of under-the-table payments further complicates the analysis. In net, Nixon (1997) argues that the deterrent effect on divorce is likely to be larger.
Nixon (1997) estimates the effect using cross-sectional variation from two March—April CPS matches. She finds a negative and robust, but small, effect of child support enforcement. For the largest of her proxies, a 1 percent increase in child support enforcement only decreases the probability of divorce by 0.16 percent (or, assuming linearity, a 10 percent increase would decrease the probability of divorce by 1.6 percent). Even given the baseline divorce rate of 12 percent, this is not a large effect. Note, however, that with only two years of CPS data, Nixon does not have sufficient variation to estimate a full DoD specification. As discussed in Chapter 3, her analysis is thus potentially biased by unmeasured state-specific characteristics that are correlated with the policies implemented.
Heim (2001) explores the effect of child support enforcement on the annual state-specific divorce rate using Vital Statistics data for 1989 to 1995. These data allow him to include a full DoD specification (i.e., fixed effects for state and year). He specifies five proxies for child support enforcement, child support collections, paternity establishment, efforts to find fathers, and average child support orders. Like Nixon, when no state fixed effects are included, child support enforcement is found to decrease divorce. However, once state fixed effects are included, there is no statistically significant effect of child support enforcement on divorce.
7.3.2. Fertility
Four econometric studies explore the effect of welfare reform on fertility (see Panel C of Table 7.3 and Table 7.4). Kearney (2001) estimates the effect of the family cap using DoD methods (with state-specific time trends) and birth certificate data. She finds no systematic effect of the family cap (see Panel C of Table 7.3). The point estimate is very small as is the standard error, so that the basic analysis can reject an effect of even 0.5 percent. This conclusion is robust to the inclusion of state-specific time trends, alternative coding of the family cap, alternative timing of the effect on fertility, using the birth rate rather than the number of births, and the inclusion of lead effects (which as expected are zero). Analyses by parity, race-ethnicity, and age (not shown) also show no consistent evidence for an effect of the family cap. In specifications that disaggregate by race, education, marital status, and parity, the point estimates for additional births to high school dropouts age 20 to 34 are positive and significant for blacks (p < 0.10) and whites (p < 0.01) for both marital and nonmarital births but not significant for other groups (high school graduates and first births). Estimates for teenagers are positive and significant (p<0.01) for additional births to unmarried blacks, but insignificant for the other groups (first births to unmarried blacks, married blacks, and whites).
While not the primary focus of her analysis, Kearney includes dummy variables for any waiver and time limits in some of her models. Like the results for the family cap, her results provide no evidence of an effect of either any waiver or a time limit on fertility. The point estimates are small and not significantly different from zero.
Levine (2001) estimates DoD models of births and birth rates using Vital Statistics data. His basic models including state-specific time trends suggest that welfare reform as a bundle decreases the birth rate by about 3 percent (and is highly significant). However, if this result were causal, we would expect it to be larger for the less educated, who are more likely to receive welfare. Levine, however, finds the effect is constant or grows with education. Thus, this pattern across subgroups suggests caution in interpreting the estimated negative effect as causal. Levine also considers the effect of the family cap. In his models with state-specific time trends, he finds that, contrary to the theory, the family cap raises fertility (and the effect is clearly statistically significant), and the effect is consistent across the age, education, and parity subgroups. Finally, Levine uses the same methods and Alan Guttmacher Institute data on abortions (see Panel D of Table 7.3). He finds no evidence of an effect of any waiver or a time limit on the abortion rate. Furthermore, these results are consistent with disaggregation by age. The data do not allow disaggregation by education or parity.
Kaushal and Kaestner (2001) use CPS data to estimate the effect of time limits, the family cap, and welfare reform as a bundle (characterized as "low intensity," "medium intensity," and "high intensity"). Their estimates can be interpreted as a restricted difference-of-difference-of-differences (DoDoD) specification; they include year and state fixed effects, and they interact the policy with a dummy variable for the population assumed to be most affected by welfare reform.61 Their first affected group is appropriate for considering effects of fertility potentially leading to welfare entry. It consists of unmarried women with 12 or fewer years of education, with two alternative corresponding unaffected groups–married women with 12 or fewer years of education and unmarried women with an associate degree. Their second affected group is appropriate for considering the effects of a family cap on subsequent fertility. It considers unmarried women with at least one child and 12 or fewer years of schooling, with two alternative corresponding unaffected groups–married women with children and 12 or fewer years of schooling and unmarried women with children and an associate degree. Their findings are not consistent with an effect of welfare reform on fertility. Across each of the individual policies they consider–time limits and family caps–and across each of the four comparison groups they consider, they find no statistically significant effect.
Kaushal and Kaestner do find effects of reform bundles, but the sign patterns are difficult to interpret. The theory suggests that reform should lower fertility. However, the only statistically significant negative effect is for low-intensity reforms and then only for the first comparison group. If there were truly an effect of reform, we would expect to find larger (in absolute value) effects with more-intensive reforms. Kaushal and Kaestner, however, find no statistically significant effect of medium-intensity reforms. Furthermore, against the theory, for their first and second comparison groups high-intensity reforms increase fertility (p < 0.05 and p < 0.10, respectively).
Finally, Horvath and Peters (1999) explore the effect of waivers on a different outcome (see Table 7.4). While the previously discussed studies analyze fertility (number of births or the birth rate), Horvath and Peters analyze the nonmarital fertility ratio, defined as the fraction of births that are to unmarried women. They compute the marital fertility ratio from Vital Statistics data (i.e., from birth certificates), and their models include state and year fixed effects. As seen in Table 7.4, they find that any implemented waiver decreases the nonmarital fertility ratio in all subgroups, teenagers and nonteenagers, whites and blacks. In almost all specifications, the effect is statistically significant at the 5 percent level or better.
| Welfare Waiver Policy Variable (Implemented) | |||||||||||
|---|---|---|---|---|---|---|---|---|---|---|---|
| Any waiver | Family Cap | Time Limit | Work Requirement | Expanded Income Disregard and Asset Limit | AFDC-UP Expansion | Strengthen Child Support | Minor Parent Provision | School Attendance and Performance Requirement | |||
| Study | Data (Years) | Outcome | Marginal effect (t-statistic) % effect |
Marginal effect (t-statistic) % effect |
Marginal effect (t-statistic) % effect |
Marginal effect (t-statistic) % effect |
Marginal effect (t-statistic) % effect |
Marginal effect (t-statistic) % effect |
Marginal effect (t-statistic) % effect |
Marginal effect (t-statistic) % effect |
Marginal effect (t-statistic) % effect |
| Horvath and Peters (1999) | State-level vital statistics (1984-1996) |
Non-marital birth ratio for women 15-19 |
-0.011 (1.99) -1.6% | -0.052 (3.55) -7.6% | -0.092 (3.70) -13.5% | 0.008 (0.59) 1.2% | -0.001 (0.03) -0.1% | -0.075 (4.83) -11.0% | 0.035 (2.16) 5.1% | 0.143 (6.06) 21.0% | 0.018 (1.88) 2.6% |
| Non-marital birth ratio for white women 15-19 | -0.014 (2.11) -2.4% | -0.058 (3.28) -10.0% | -0.102 (3.40) -17.6% | 0.001 (0.59) 0.2% | 0.003 (0.18) 0.5% | -0.078 (4.15) -13.4% | 0.041 (2.08) 7.1% | 0.167 (5.87) 28.8% | 0.009 (0.74) 1.6% | ||
| Non-marital birth ratio for black women 15-19 | -0.012 (2.24) -1.4% | -0.024 (1.63) -2.8% | -0.104 (4.08) -12.0% | 0.003 (0.23) 0.3% | -0.002 (0.12) -0.2% | -0.047 (2.98) -5.4% | 0.008 (0.51) 0.9% | 0.115 (4.88) 13.2% | 0.008 (0.83) 0.9% | ||
| Non-marital birth ratio for women 20-49 |
-0.008 (3.43) -3.8% | -0.032 (5.55) -15.2% | 0.0001 (0.01) 0.0% | 0.004 (0.63) 1.9% | 0.011 (2.03) 5.2% | -0.019 (2.73) -9.0% | 0.022 (4.19) 10.5% | ||||
| Non-marital birth ratio for white women 20-49 | -0.006 (3.10) -4.3% | -0.024 (4.60) -17.1% | -0.010 (1.06) -7.1% | 0.001 (1.64) 0.7% | 0.004 (0.86) 2.9% | -0.006 (0.97) -4.3% | 0.022 (4.68) 15.7% | ||||
| Non-marital birth ratio for black women 20-49 | -0.016 (3.72) -3.1% | -0.038 (3.38) -7.5% | -0.045 (2.25) -8.8% | -0.003 (0.31) -0.6% | 0.016 (1.40) 3.1% | -0.023 (1.70) -4.5% | 0.040 (3.78) 7.8% | ||||
| NOTE: Dependent variable is log of odds ratio transformations
of race and age group specific ratios of non-marital births to total
births for each state. Coefficients transformed to reported marginal
effect. Absolute value of t-statistic in parentheses. Regressions
are weighted by state population due to heteroskedasticity, and lagged
nine months to account for natural lag associated with childbearing.
All models include state and year fixed effects and the following controls: state poverty rate; race-specific female unemployment rate; race-specific teenage unemployment rate; race and gender-specific wages; number of AIDS cases weighted by state population; ratio of whites to blacks in state population; number of abortion providers per 1000 women of childbearing age; fundamentalist adherents as proportion of state population; high school completion rate among 18-24 yr. olds not currently in high school; proportion of population living in urban area; race and age-specific marriage market opportunities; percent of children in single parent homes lagged 24 years (post-teen regressions only); race-specific ratio of teen births lagged 17 years (teen regressions only); maximum welfare plus food stamp benefit for a family of three; sex education required in public schools; and parental consent required for teen abortion (teen regressions only). |
They also present results for the impact of specific waiver policies on the nonmarital birth ratio. Family caps are estimated to lower the nonmarital fertility rate among teenagers by 6 percentage points for whites and 2 percentage points for blacks; for adults age 20 and above, the corresponding effects for whites and blacks are 2 and 4 percentage points. With the exception of the black teenager effect (significant at the 10 percent level), these effects are statistically significant at the 5 percent level.
These results for the effects of the family cap diverge from those found in the other observational studies. One possible explanation is that Horvath and Peters analyze the nonmarital fertility ratio, while the other studies analyze births or the birth rate. Kearney (personal communication 3/12/02) reports that when she applies her basic models to the nonmarital fertility rate, she does not find an effect of the family cap. Thus, it seems unlikely that the different outcome explains the divergence. Kearney also notes that Horvath and Peters do not appear to have adjusted for changes in the coding of marital status during this period, and that their coding of waivers differs substantially from those used in other studies.
Horvath and Peters also find effects for other specific waivers. The magnitudes are often even larger than these effects for the family cap, but they sometimes have the opposite of the expected sign. Consistent with the expectation, time limit waivers decrease the nonmarital fertility ratio by 10 percentage points for teenagers, and 5 percentage points for black adults. AFDC-UP expansion waivers also decrease the nonmarital fertility ratio, especially for teenagers and especially for white teens (effects as high as 8 percent). Waivers to strengthen child support raise the nonmarital fertility ratio (by 2 to 4 percentage points for adults and teens, respectively). This would be the expected sign if women were now more confident of support from the father; but not if fathers were now more cautious about conceiving a child. Counter to intuition, however, minor parent provisions are estimated to raise the nonmarital fertility ratio by over 10 percentage points, with effects that are statistically significant at the 5 percent level or better. Finally, work requirement waivers, benefit structure waivers, and school attendance and performance requirement waivers appear to have no effect (almost all the estimated effects are statistically insignificant and small in magnitude).
7.4. EVALUATING THE EFFECTS OF WELFARE REFORM ON FAMILY STRUCTURE
In this section we synthesize the findings from experimental and econometric studies that aim to measure the impact of welfare reform on marriage and fertility, the two outcomes that are the focus of the bulk of the studies that consider family structure impacts. We first discuss impacts for specific reform policies, and then for welfare reform as a bundle.
7.4.1. Effects of Specific Reforms
The demonstration studies provide the strongest basis for assessing the impact of specific reforms on the family structure decisions of current recipients (but not on potential entrants); yet, the reform policies that can be evaluated are somewhat limited. Strong financial work incentives alone and, when tied to hours worked, or in combination with mandatory work-related activities, have only been evaluated in terms of their impact on marriage. None of the demonstrations that combine weaker incentives with work requirements consider either marriage or fertility. While programs with TANF-like bundles of reforms have evaluated both marriage and fertility, they do not allow us to draw solid inferences about the marginal contribution of the time-limit feature. As might be expected, family caps have only been evaluated in terms of their impact on fertility, but as the earlier discussion reveals, the studies with this focus have a number of potential flaws. It is striking that we have the most evidence regarding the impact of work requirements on marriage and fertility since these policies might be expected to have the weakest impact on these outcomes, and the evidence indeed bears this out.
Marriage
Based on the results presented in Section 7.2, there does not appear to be any effect of mandatory work-related activities on marriage. The fact that nearly all the impact estimates are statistically insignificant and almost evenly divided in their sign suggests that work activity requirements alone have no effect on marriage rates.
The findings from the studies that evaluate the impact of financial work incentives present a number of puzzles. The findings for MFIP provide some evidence that financial work incentives can raise marriage, but these findings are not consistent for recipients and applicants, and there are differences when the program is limited to the financial work incentives component. In interpreting the MFIP findings, it is important to note that MFIP did more than simply enhance the financial work incentives of the welfare program. It also broadened eligibility for AFDC-UP and changed the treatment of stepparent earnings.
The MFIP-IO results suggest that strong financial work incentives alone may raise marriage rates, at least for recipients. When combined with mandatory work requirements, MFIP still produces positive impacts on marriage, for both recipients and applicants, but they are no longer statistically significant. In addition, the two-parent sample in MFIP demonstrated a large and significant impact on the likelihood of staying married. For the MFIP two-parent sample, almost all these cases had a married spouse present at the time of randomization. The control group means suggest that three years later, less than half are still married. Thus, there is considerable potential for improvement simply by maintaining the current marital status. In contrast, while there is considerable scope for improving marriage rates among the one-parent cases, such an improvement would require a change in marital status (rather than simply maintaining the previous status).
Another puzzle is associated with the findings for SSP. In that case, there is no significant impact on marriage for the pooled sample, but significant and opposing effects for the two study areas, British Columbia and New Brunswick. (Unlike MFIP, there are no two-parent results for SSP.)
As a whole, these results suggest the possibility that financial work incentives alone or in combination with mandatory work-related activities may both promote marriage and discourage divorce. There is, however, evidence in the opposite direction from British Columbia. Given the prominent role of marriage in PRWORA, additional random assignment evaluation of the effect of financial work incentives on marriage seems warranted.
Fertility
As with marriage, it appears that there is no impact of mandatory work-related activities on fertility behavior. The individual point estimates are not statistically different from zero, and they are of both signs.
In contrast to financial work incentives, work requirements, and time limits, family caps were instituted with the express goal of reducing subsequent childbearing for those already on aid. Here also, the evidence is mixed. One experimental study (AWWDP) finds no effect; another (FDP) finds a large negative effect. One observational study (Horvath and Peters, 1999) finds a decrease in the fraction of births that are nonmarital; three other studies find no effect (Kearney, 2001; Kaushal and Kaestner, 2001; Levine, 2001).
The quality of the studies that evaluate family caps is not uniform. While random assignment usually yields robust estimates of policy effects, the methodological issues surrounding the two random assignment analyses of family caps are so severe as to require that those results be strongly discounted. Among the observational studies, Horvath and Peters (1999) appear to be the outlier, and Kearney does not find an effect even when she uses the nonmarital fertility ratio. Thus, the available evidence appears to be inconsistent with an effect of the family cap on fertility.
7.4.2. Effects of Reform as a Bundle
The econometric studies and random assignment studies that evaluate TANF-like bundles of reform present a mixed picture of the overall effect of welfare reform on marriage. The econometric studies summarized in Section 7.3 generally suggest that welfare reform as a bundle increases marriage. The econometric studies provide evidence of both negative and positive effects, again typically small in magnitude. Of these studies, only ABC finds a positive impact on marriage, and it is marginally statistically significant. This is also the only study to look at subgroup differences and provides some indication that the positive impacts for marriage may be strongest for younger, less educated women who have yet to marry as of random assignment.
It is not clear why ABC’s findings differ from either FTP or Jobs First with which it is most directly comparable. FTP and Jobs First share similar and sometimes stricter features with ABC (for example, the shorter time limit in Jobs First), although the sanctions in ABC may be viewed as stronger and the financial incentives weaker. In terms of other areas of program impact, ABC and Jobs First had similar impacts on earnings (see Table 5.1). As we will see next in Chapter 8, ABC had no impact on a broader measure of income. In contrast, FTP and Jobs First each have sizeable positive impacts, at least prior to time limits becoming binding (see Table 8.1). The absence of any income gains in ABC may provide part of the explanation. In fact, Fein (1999) associates the positive marriage impact for ABC with work requirements and strong sanctions that placed pressure on women to find alternative sources of income support. If FTP and Jobs First allowed women to increase income on their own, at least prior to time limits setting in, they may depress marriage rates relative to a program like ABC, which has no impact on recipient income.
The evidence on fertility is also mixed. The evidence from econometric studies with respect to reform as a bundle is not consistent, with studies suggesting no effect or a negative impact. As we have discussed in other chapters, the lack of statistically significant impacts for TANF as a bundle on family structure may be the result of limited variation in the timing of the implementation of TANF across states. When models include state and year fixed effects, there is too little variation left to precisely estimate TANF effects.
The random assignment studies that evaluate TANF-like bundles of reform also find no consistent impact on fertility, with a mixture of positive and negative insignificant impacts for the case head. The one exception is the statistically significant negative impact on births and conceptions to unwed minors found in EMPOWER. Arizona had other reforms that may explain the fertility impact for minors, namely a family cap, a minor residency requirement, and a requirement for teen JOBS participation. However, the separate impact of these provisions is not known.
7.5. CONCLUSIONS
TANF and the welfare reforms under waivers in the pre-TANF period aimed specifically to change family formation–to increase marriage, to decrease separation or divorce, and to decrease nonmarital fertility. Unfortunately, with the exception of mandatory work-related activities, the research base is comparatively weaker than for outcomes considered in earlier chapters. We, therefore, are more limited in our ability to draw firm conclusions about the impact of specific reform policies or welfare reform as a bundle on family structure. Furthermore, marriage and fertility may be two outcomes where the impact of welfare reform policies will be more pronounced over a longer horizon than what is available with most of our current research base.
In terms of marriage, the evidence from both random assignment and econometric studies is insufficient to draw any conclusions about the effect of welfare reform as a bundle. In terms of specific policy reforms, the experimental studies are quite clear that there is no effect of programs that focus on work-related activities. There is some suggestive evidence from MFIP that programs that provide generous financial work incentives, either alone or with work requirements, may increase marriage or keep existing marriages intact. However, the mixed results for the Canadian SSP suggest caution in interpreting the MFIP results. The contrast with the earlier Negative Income Tax Experiments suggests that those interested in affecting marital status through welfare policy give careful consideration to the relative attractiveness of welfare programs for one-parent and two-parent cases. Relevant program features may include who keeps the benefits if the marriage breaks up and how a new partner’s earnings (perhaps not the father of the child) would affect the benefit received.
Likewise, for fertility, the evidence on whether there is an effect of welfare as a bundle on fertility is inconclusive, and the demonstration studies are quite clear that there is no effect of work-related activities programs. There is no basis for evaluating the effect of financial work incentives alone or in combination with mandated work-related activities on fertility. The available evidence on the family cap is limited and contradictory, but the best of the studies finds no effect.
55The "100-hour rule" under AFDC required that, in addition to being financially eligible for benefits, the primary wage-earner could work no more than 100 hours per month. To meet the work history requirement, the family also had to show that the primary wage-earner had earned at least $50 in at least 6 of the last 13 calendar quarters or had been eligible for unemployment compensation during the past year.(back)
56Under AFDC-UP, welfare was potentially available to two-parent families only when there was substantial previous labor market experience (six of the last thirteen quarters, but less than 100 hours of work in the current month). This condition made it unlikely that teens or young two-parent families would qualify.(back)
57This use of survey data is in contrast to most of the analyses of the previous chapters (considering welfare use, employment and earnings, and use of other government programs), but like most of the analyses in later chapters (considering income, other measures of well-being, and child development). As discussed below, population level analyses of fertility have access to Vital Statistics/birth certificate data. Like administrative data, birth certificate data are available for the entire population (not just a sample), in every time period, and without recall bias. However, only aggregate birth certificate data are available. No study has matched experimental data to individual-level birth certificate data, so random assignment analyses cannot use these data.(back)
58In Canada, couples who live together for at least one year and are not legally married are considered common-law partners, with rights that are akin to marriage (Michalopoulos et al., 2000).(back)
59Although we rely throughout our analysis on MFIP results for the urban sample only, results for the pooled urban and rural MFIP single-parent recipient sample show a somewhat larger positive marriage impact (10.6 percent currently married and living with the spouse in the treatment group versus 7.0 percent in the control group), a difference of 3.6 percentage points that is statistically significant at the 5 percent level (Miller et al., 2000). There is no statistically significant impact on the same measure for the pooled sample of urban and rural single-parent applicants (and the impact estimate is actually negative). In contrast to the pooled result, the lack of significance for the subset of urban single-parent recipients reported in Table 7.1 may be due to the small sample sizes (less than 400 in each of the treatment and control groups).(back)
60In addition, a small number of cases (21, well under 1 percent of the control cases) were informed that they were subject to the family cap when they were not.(back)
61With three levels, the full DoDoD specification would include not merely state and year fixed effects, but a fixed effect for every state-year combination. They do estimate that model.(back)
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