Table of Contents | Previous | Next |
Chapter Four
THE CASELOAD AND WELFARE USE
4.1. BACKGROUND
We begin the core synthesis chapters by analyzing the effects of welfare reform on welfare use. Of all the welfare-related outcomes we consider, welfare use may be most directly affected by reform. It has also received the most research attention. Much of this attention stems from the dramatic changes in welfare caseloads that took place during the 1990s.
Figure 4.1 presents data for the period 1970 to 2001 on the welfare caseload, defined as the fraction of the U.S. population receiving cash aid (either under AFDC or TANF). For most of that period, the caseload was fairly stable. However, beginning in the late 1980s, it increased substantially, rising from 4.5 percent to 5.5 percent between 1988 and 1993. After 1993, caseloads started falling. By 2000, they had reached 2.1 percent, a 35-year low. As of June 2001, they remained at that level.
|
[D] |
Many studies have attempted to explain this precipitous decline. One suggested explanation is the economy. A useful measure of economic conditions is the unemployment rate, which is also plotted in Figure 4.1. Prior to 1990, changes in the welfare caseload were weakly associated with changes in the unemployment rate, as evidenced by the small increases in the caseload during the 1975 and 1980 recessions. The eligibility restrictions in OBRA 1981 have been offered to explain why caseloads did not rise further as unemployment approached 10 percent, in the early 1980s, but the caseload also remained roughly constant during the earlier recession. Only since 1990 have changes in the caseload closely tracked changes in the unemployment rate. Both increased sharply during the early 1990s and decreased sharply thereafter. In 2001, due to the softening economy, the unemployment rate rose to 4.8 percent.
Another suggested explanation for the drop in welfare caseloads is welfare reform. The caseload decline coincides with sharp increases in the number of states reforming their welfare programs, first under waivers and then under PRWORA. As shown in Figure 4.1, the first statewide waivers were implemented in 1992; by 1998, all states had implemented their TANF plans.
The role played by welfare reform is the topic of what follows. Estimates of the effects of welfare reform from a number of random assignment studies are the subject of the next section. That section also includes a brief summary of the results discussed in Appendix A regarding subgroup differences in the impacts of reform policies on the welfare caseload. Following that, we discuss the results from a number of econometric studies. In section 4.4, we synthesize the studies to convey what is known about the effects of welfare reform on welfare use. We conclude with a summary of our findings.
4.2. RANDOM ASSIGNMENT STUDIES OF THE EFFECTS OF WELFARE REFORM ON WELFARE USE
The estimates that we report for the random assignment studies are typically referred to as "impact" estimates. They represent the difference between the average welfare-related outcome among the treatment group and the average welfare-related outcome among the control group. The precise outcome measures, and the follow-up period over which they are calculated, vary from study to study and are reported in column (4) of Table 4.1. The impact estimates themselves appear in column (6). Column (7) reports percentage impacts, obtained by dividing the impact estimates by the control group means in column (5).
For several studies, we report more than one estimate. The reason is that most studies report estimates that are disaggregated in various ways. The most common disaggregations involve ongoing recipients versus new applicants. Where possible, we present separate results for these groups. In many cases, however, the original study presents the results only in aggregated form.30
For some programs, we present results for different time periods following random assignment. We do this when the program impacts seem to change over time. We also report multiple results when the program’s effect on other outcomes, such as employment, changes over time. This facilitates comparisons across outcomes in later chapters. Finally, we present multiple results for the few studies that report impacts for periods both before and after their time limits become binding.
Where possible, we report in Table 4.1 estimates based on single-parent families, which are the largest group to receive welfare. In a few studies, both single-parent and two-parent families participated, but results were not reported separately. In those cases, we present the overall estimates. Since the single-parent group is so much larger than the two-parent group, that group tends to dominate those results.
4.2.1. Programs That Focus on Financial Work Incentives
As indicated in Chapter 3, three studies provide information on the effects of financial work incentives: CWPDP, WRP, and MFIP. Extended financial work incentives were one of the main reforms included in CWPDP, although the program impacts also reflect the effects of the program’s reduced benefit level. WRP and MFIP were dual-treatment experiments. The treatment groups for the full WRP and full MFIP programs were subject to both work-related activity mandates and financial work incentives, whereas the Incentives Only treatment groups, WRP-IO and MFIP-IO, were subject only to the financial work incentives.31
| Welfare use | ||||||
|---|---|---|---|---|---|---|
| Name | Cases served | Data | Measure | Control mean | Impact | % |
| A. Programs that focus on financial work incentives | ||||||
| CWPDP | Single parent recipients | A | Avg. welfare receipt, year 3 | 67.0 | 1.0 | 1.5% |
| WRP-IO | Single-parent recipients and applicants | A | Ever received welfare, last 3 mos. of FU | 37.4 | 0.3 | 0.8% |
| MFIP-IO | Urban single parents recipients | A | Avg. quarterly welfare receipt, year 1 | 90.7 | 2.8*** | 3.1% |
| A | Avg. quarterly welfare receipt, year 3 | 63.6 | 10.5*** | 16.5% | ||
| Urban single parents applicants | A | Avg. quarterly welfare receipt, year 1 | 65.8 | 8.4*** | 12.8% | |
| A | Avg. quarterly welfare receipt, year 3 | 36.6 | 10.3*** | 28.1% | ||
| B. Programs that focus on financial work incentives tied to hours of work | ||||||
| New Hope | Poor families employed FT at RA | A | Months receiving welfare, year 1 of 2-yr FU | 3.4 | -0.1 | -2.9% |
| A | Months receiving welfare, year 2 of 2-yr FU | 2.6 | -0.8** | -30.8% | ||
| Poor families not employed FT at RA | A | Months receiving welfare, year 1 of 2-yr FU | 5.9 | 0.0 | 0.0% | |
| A | Months receiving welfare, year 2 of 2-yr FU | 3.6 | 0.3 | 8.3% | ||
| SSP | Single-parent recipients | A | Monthly receipt of IA or SSP year 2 | 78.9 | 7.6*** | 9.6% |
| A | Monthly receipt of IA or SSP year 3 | 70.7 | 9.8*** | 13.9% | ||
| SSP Plus | Single-parent recipients | A | Receipt of IA or SSP, Q5 | 81.1 | 4.3 | 5.3% |
| SSP Applicants | Single-parent applicants | A | Receipt of IA or SSP, Q5 | 61.5 | 3.7** | 6.0% |
| A | Receipt of IA or SSP, Q9 | 49.6 | 6.4*** | 12.9% | ||
| C. Programs that focus on mandatory work-related activities | ||||||
| LA Jobs-1st GAIN | Single-parent recipients and applicants | A | Received welfare, Q8 | 66.2 | -4.6*** | -6.9% |
| Atlanta LFA | Recipients and applicants | A | Received welfare, Q8 | 67.0 | -5.7*** | -8.5% |
| Grand Rapids LFA | Recipients and applicants | A | Received welfare, Q8 | 60.9 | -7.4*** | -12.2% |
| Riverside LFA | Recipients and applicants | A | Received welfare, Q8 | 56.4 | -6.4*** | -11.3% |
| Portland | Recipients and applicants; no cases with substantial barriers | A | Received welfare, Q8 | 53.0 | -11.7*** | -22.1% |
| Atlanta HCD | Recipients and applicants | A | Received welfare, Q8 | 67.0 | -3.5** | -5.2% |
| Grand Rapids HCD | Recipients and applicants | A | Received welfare, Q8 | 60.9 | -6.5*** | -10.7% |
| Riverside HCD | Recipients and applicants | A | Received welfare, Q8 | 60.0 | -4.1** | -6.8% |
| Columbus Integrated | Recipients and applicants | A | Received welfare, Q8 | 53.0 | -6.8*** | -12.8% |
| Columbus Traditional | Recipients and applicants | A | Received welfare, Q8 | 53.8 | -4.6*** | -8.6% |
| Detroit | Recipients and applicants | A | Received welfare, Q8 | 73.7 | -3.6*** | -4.9% |
| Oklahoma City | Applicants | A | Received welfare, Q8 | 40.8 | -2.5** | -6.1% |
| IMPACT Basic Track | Recipients and applicants-basic track | A | Received welfare, Q4 | 52.4 | 2.2 | 4.2% |
| D. Programs that focus on financial work incentives and mandatory work-related activities | ||||||
| WRP | Single-parent recipients and applicants | A | Ever received welfare, last 3 mos. of FU | 37.4 | -2.1 | -5.6% |
| MFIP | Urban single-parent recipients | A | Avg. quarterly welfare receipt, year 1 | 90.7 | 1.7* | 1.9% |
| A | Avg. quarterly welfare receipt, year 3 | 63.6 | 7.6*** | 11.9% | ||
| Urban single-parent applicants | A | Avg. quarterly welfare receipt, year 1 | 65.8 | 8.4*** | 12.8% | |
| A | Avg. quarterly welfare receipt, year 3 | 36.6 | 6.4*** | 17.5% | ||
| TSMF | Recipients | A | Monthly welfare receipt over 4-yr FU | 60.4 | -1.5*** | -2.5% |
| Applicants | A | Monthly welfare receipt over 1-yr FU | 64.1 | -2.1 | -3.3% | |
| A | Monthly welfare receipt over 2-yr FU | 54.7 | -1.9** | -3.5% | ||
| FIP | Recipients | A | Welfare receipt, Q4 | 76.2 | 3.3*** | 4.3% |
| A | Welfare receipt, Q8 | 57.3 | 1.3 | 2.3% | ||
| Applicants | A | Welfare receipt, Q4 | 34.8 | 2.2 | 6.3% | |
| A | Welfare receipt, Q8 | 23.8 | 1.2 | 5.0% | ||
| 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 (a) | Recipients | A | Monthly welfare receipt, months 1-36 | 41.1 | -1.0 | -2.4% |
| IMPACT Placement Track |
Recipients and applicants-placement track | A | Received welfare, Q4 | 52.6 | -9.3*** | -17.7% |
| A | Received welfare, Q8 | 29.3 | -3.9 | -13.3% | ||
| VIP/VIEW | Recipients | A | Welfare receipt in Q8 | 53.3 | -1.2 | -2.3% |
| ABC | Recipients and applicants | A | Months on welfare, Q1-Q4 | 9.1 | 0.0 | 0.0% |
| FTP | Recipients and applicants | A | Avg. percent receiving aid, year 2 | 44.4 | -0.8* | -1.8% |
| A | Avg. percent receiving aid, year 3 | 32.0 | -6.9*** | -21.6% | ||
| A | Avg. percent receiving aid, year 4 | 20.7 | -8.8*** | -42.5% | ||
| JOBS First | Recipients and applicants | A | Ever received aid, Q7 | 53.9 | 6.8*** | 12.6% |
| A | Ever received aid, Q8 | 51.0 | -5.7*** | -11.2% | ||
| A | Ever received aid, Q16 | 28.0 | -9.3*** | -33.2% | ||
| NOTES: For full program names and citations, see
Table 3.4. Abbreviations: A=administrative data; S=survey data; FU=follow-up;
HH=household; Q=quarter; RA=random assignment; FT=full-time. * = 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. |
According to the economic model discussed in Chapter 3, financial work incentives should increase employment. Both CWPDP and WRP-IO increased welfare use slightly, but neither impact was significant. In contrast, the results from MFIP-IO show sizeable and significant increases in welfare use among both ongoing recipients and new applicants.
The different results generated by these different programs potentially could be explained by a number of factors. However, one particularly important difference is in the generosity of the programs’ financial work incentives, as seen in Table 3.5. Both CWPDP and WRP involved fairly weak financial work incentives. In CWPDP, the treatment and control groups were subject to the same earnings disregards during the first four months of employment; the treatment group experienced more generous financial work incentives only after working for four months. The WRP treatment group actually faced a higher benefit reduction rate than the control group during the first four months of work. Moreover, the differential incentive remained fairly small during the fifth through twelfth months of work. In contrast, the MFIP incentive was fairly generous, which may explain why it had a relatively strong effect.
4.2.2 Programs That Focus on Financial Work Incentives Tied to Hours of Work
The programs listed in Panel B of Table 4.1 involve financial work incentives in the form of earnings supplements that are conditioned on full-time work. In all cases, the earnings supplement is paid outside the welfare system. As a result, these programs may be thought of as alternatives to traditional welfare.
The New Hope program had little effect on AFDC use among families not working full-time when randomly assigned, but it did significantly decrease second-year AFDC receipt among families initially satisfying the full-time work requirement. Unfortunately, Bos et al. (1999) do not report how New Hope affected the rate of transfer receipt, that is, the rate at which the treatment group received support from either AFDC or the earnings supplement. They report that 74 percent of the treatment group received the supplement at some point over the 24-month follow-up period, making it likely that the program raised the rate of transfer receipt. However, they do not report supplement receipt in a way that would allow us to eliminate possible double counting of persons receiving both types of aid. Thus, we cannot say for certain whether the results from New Hope accord with the standard economic model, which predicts that the total transfer rate should rise.
The SSP programs all raised the total transfer rate, that is, the rate at which recipients received either traditional welfare (Income Assistance, or IA) or the SSP supplement. Only in the SSP Plus program, where the sample size was small (596), was the effect insignificant. SSP decreased IA receipt (not shown), but the total transfer rate increased by virtue of the number of participants willing to work full time in exchange for the supplement.
4.2.3. Programs That Focus on Mandatory Work-Related Activities
Panel B of Table 4.1 reports on 13 welfare-to-work programs. Eleven are part of NEWWS; the others are L.A. Jobs-First GAIN and Indiana’s IMPACT program Basic Track.
The welfare-to-work programs in all but one of the sites resulted in lower levels of welfare use. This is largely consistent with the predictions that work requirements should make welfare less attractive from the standard economic model discussed in Chapter 2. The average reduction in welfare use is 5.1 percentage points. Relative to the control-group mean, the average reduction is 8.7 percent.
Across the programs, there is evidence that the job-search-oriented programs generated somewhat greater reductions in welfare use than the skills-oriented programs during the first two years of the follow-up. The job-search-oriented programs–L.A. Jobs-First GAIN, Atlanta Labor Force Attachment (LFA), Grand Rapids LFA, and Riverside LFA–reduced welfare use by an average of 6 percentage points, whereas the skills-oriented programs–Atlanta Human Capital Development (HCD), Grand Rapids HCD, Riverside HCD, and the programs in Columbus, Detroit, Oklahoma City, and Indiana–averaged 3.9 percentage-point reductions. Moreover, in the three NEWWS sites that ran both an LFA and an HCD program, the LFA programs had larger effects on welfare use. The Portland program had the largest effects of all, which may bode well for its hybrid model. Then again, Portland’s larger effects may be attributable to the fact that, unlike the other sites, the Portland program excluded recipients with substantial barriers to employment from participating in the demonstration (Freedman et al., 2000a, p. ES-21). The Detroit, Oklahoma City, and Indiana programs yielded the smallest reductions in welfare use, which may be attributable to lower levels of enforcement. Both Columbus programs yielded similar effects, providing no clear evidence that alternative case management approaches matter.
Recent data from NEWWS provide information on the longer-term effects of mandatory work-related activities. Program impacts by year after random assignment are presented in Figure 4.2. In all cases but one, the effects of the program fade over time: The longer-term impacts are smaller than the shorter-term impacts.32
|
[D] |
4.2.4. Programs That Focus on Financial Work Incentives and Mandatory Work-Related Activities
Panel D of Table 4.1 presents results from four programs that combine financial work incentives with mandatory work-related activities. Whether these programs raise or lower welfare use cannot be predicted from the theoretical framework discussed in Chapter 2. By themselves, work mandates should decrease welfare use, whereas financial work incentives should increase it. Thus, the net effect will depend on the relative strength of the two opposing influences.
Of the four programs, WRP and TSMF reduced welfare use (albeit insignificantly in the case of WRP), whereas MFIP and FIP increased it. As can be seen from Table 3.5, the two programs that increased welfare use also had relatively generous financial work incentives; the other two programs had less generous financial work incentives. Although other factors could contribute to the differences as well, the impacts are generally consistent with the notion that the effects of financial work incentives are most likely to dominate the effects of work mandates when the financial incentives are strong.
4.2.5. Programs That Focus on TANF-Like Bundles of Reforms
The six programs listed in Panel F of Table 4.1 combine time limits with work-related activity mandates (EMPOWER and the IMPACT Placement Track), financial work incentives (FTP), or both (VIP/VIEW, ABC, and Jobs First). Because they include a number of major reforms, these programs may be the most similar to the TANF plans adopted by the states after the passage of PRWORA. These programs provide some insights into the effects of reform as a bundle, although their broad focus makes it difficult to isolate the effects of any specific reform from the general program impacts. However, two of them do shed some light on what happens when families begin to reach the time limit.
Implementation issues bear on the interpretation of the impact estimates from a number of these studies. For example, in Virginia, although the implementation of the VIEW reforms took place at different times in different counties, the data on which the analysis is based pertain to the same time period for all of the study sites. Thus, the sample period includes both pre-reform and post-reform data. In fact, in two of the sites, it includes only pre-reform data, since VIEW was implemented there in the last month of the sample period. The presence of pre-reform data would tend to mask the effects of the program, since the pre-reform behavior of the treatment and control groups should be the same if randomization is carried out properly. As a result, we pay the VIP/VIEW results relatively little attention, both here and in later chapters.33
There are further questions about the extent to which these programs reflect the effects of their time limits. Most of these studies cover only the pre—time limit period, that is, the period prior to when any of the participants could have exhausted their benefits. Thus, with the exceptions of the FTP and Jobs First evaluations, these studies provide no information on the mechanical effects of time limits.
Furthermore, because of implementation issues, it is doubtful that the time limits included in these programs could have had much effect on behavior. As discussed in Chapter 3, there was substantial confusion about time limits among the study participants in the EMPOWER, IMPACT, and ABC programs. As a result, the impact estimates for these programs may reflect only the effects of their other policy reforms.
The other policy reform in EMPOWER involved changes to JOBS work-related activity mandates. However, the changes were fairly minor, amounting to a slight stiffening of sanctions for noncompliance without any changes in required activities or exemptions. This may explain why the program had essentially no effect on welfare use.
IMPACT’s Placement Track component also included mandatory work-related activities. Unlike EMPOWER, however, IMPACT imposed substantially more rigorous mandates and a search-oriented welfare-to-work program. Its impacts on welfare use are roughly comparable to those of the programs that focus solely on search-oriented work-related activities. However, only the first-year effect is significant.
Besides its poorly understood time limits, ABC involved mandatory work-related activities and a financial work incentive. The program as a whole had no effect on welfare use. It is possible that the opposing incentives of the program’s two operative reforms offset each other.
FTP also involved policy reforms with conflicting incentives for welfare use. Its 24-month time limit was relatively well understood, with 88 percent of the treatment group and 29 percent of the control group reporting that they were subject to time limits.34 The program also involved a fairly generous financial incentive. During year two of the follow-up period, FTP reduced welfare use by 0.8 percentage points. This suggests that the opposing incentives of the financial incentive and the time limit nearly offset each other, at least during the pre—time limit period.
Jobs First also provided conflicting incentives. Its 21-month time limit was well understood; 89 percent of the treatment group and 23 percent of the control group reported that they were subject to time limits. Like the time limit, its strengthened work-related activity mandate should have decreased welfare use. However, the program also included a very generous financial incentive: Members of the program group could earn up to the federal poverty line without having their benefit reduced. The strength of this financial incentive may explain why Jobs First actually increased welfare use by 6.8 percentage points during the last quarter of the pre—time limit period. Apparently, the effect of the extraordinarily generous financial incentive outweighed the effects of the work-related activities mandate and the time limit.
FTP and Jobs First are the only programs to provide insights into how TANF-like reform programs affect welfare use once the time limit begins to become binding. In FTP, the post—time limit period begins with year three; in Jobs First, it begins with quarter eight. Both programs had a sizeable reduction welfare use during the post—time limit period. Moreover, the negative impact grew over time. On the one hand, this may indicate merely that families that exhaust their benefits are indeed dropped from the rolls. On the other hand, given the substantial uncertainty surrounding the question of whether states would indeed enforce time limits, the finding that at least two states have done so is an important observation (Blank, forthcoming).
Finally, the change in welfare impacts between the pre— and post—time limit periods may shed some light on the mechanical effects of time limits. In FTP, none of the recipients could have exhausted their benefits prior to the end of year two. In Jobs First, none of the recipients could have exhausted their benefits prior to the end of quarter seven. To construct an estimate of what happens when recipients begin to reach the time limit, we subtract the pre—time limit impact from the post—time limit impact
This is not an experimental estimate of the mechanical effects of time limits, because program participants were not randomized with respect to the time at which they reached the time limit. Rather, it can be interpreted as a DoD estimate. The difference between the treatment and control groups estimates the impact of the program, and the difference between the pre— and post—time limit impacts estimates the mechanical effect of the time limit. This DoD approach will yield a valid estimate only if the effects of the programs’ other policy reforms do not change between the two periods. This condition is more likely to be satisfied the closer the time periods used to construct the estimate. For this reason, we focus on the last pre—time limit period and the first post—time limit period. However, the estimates only indicate what happens as a specific fraction of recipients reaches the time limit. The mechanical effects of time limits could become larger as more recipients exhaust their benefits.
In both cases, the impact of the program falls sharply as recipients begin to reach the limit. In FTP, the program impacts fall from —0.8 to —6.9 between years two and three. This amounts to 14 percent of the year-two control-group mean. In Jobs First, the program impact falls from 6.8 to —5.7, a relative decline of 23 percent. These are substantial changes.
4.2.6. Subgroup Differences
In Appendix A, we discuss what is known about the effects of various reforms on the welfare caseload for different segments of the welfare population. For the most part, the evidence is limited: There is little clear evidence on how the effects of the various policy reforms vary across subgroups. As for programs involving financial work incentives, there are no obvious patterns. Of the three studies involving TANF-like bundles of reform that provide subgroup estimates, there is no clear tendency for the reforms to have greater or lesser effects among the more disadvantaged. There is better evidence about programs that focus on mandatory work-related activities. This evidence suggests that such policies are similarly effective for most subgroups of the recipient population. At the same time, however, it suggests that search-oriented programs decrease welfare use among more disadvantaged groups by a somewhat greater amount than do skills-oriented programs.
4.3. ECONOMETRIC STUDIES OF THE EFFECTS OF WELFARE REFORM ON WELFARE USE
In addition to the random assignment studies, several econometric studies have attempted to estimate the effects of welfare reform. Although most of these studies focus on the effects of reforms as a bundle, several attempt to estimate the effects of specific reforms. We survey the estimates of specific reforms in Section 4.3.2 and focus on the effects of reform as a bundle in Section 4.3.3. However, we start with an overview of the similarities and differences of the econometric studies evaluated.
4.3.1. Similarities and Differences of Econometric Studies
A central challenge facing these studies is to disentangle the effects of reform from the effects of the economy. As seen in Figure 4.1, both were trending in ways that should have reduced the caseload. In the language of the research literature, such simultaneous trends are referred to as "collinear." Solving the collinearity problem, that is, distinguishing the effects of reform from the effect of the economy, has been a concern in all of the econometric analyses of welfare reform. It is an even greater problem in estimating the effects of specific reforms, since the effect of each reform must be distinguished not only from that of the economy, but also from those of the other reforms.
Most of the econometric studies are based on several years of annual state-level administrative data, most of which focus on annual state-level caseloads. Three studies directly analyze percent changes in caseloads between two points in time. Four studies are based on individual-level survey data. Two others use survey data aggregated by state, year, and various demographic measures. One reanalyzes data from the FTP demonstration.
Although these studies differ in many ways, they share some similarities. They involve regression models in which a measure of either the aggregate caseload or individual-level welfare use is to be explained by some or all the following factors: one or more measures of welfare reform, a measure of the generosity of the state’s welfare program, and one or more measures of the economy. Typically, the analysis includes the current value and possibly lagged values of the annual state-level unemployment rate to control for the economy and distinguish the effects of the economy from the effects of the reform. Studies based on individual-level data typically control for a number of individual-level characteristics known to predict welfare use, such as the mother’s age, education, race, and family size. Some of the aggregate studies also include state-level averages of such characteristics as control variables. Most of the analyses also include state-fixed effects and state-specific time trends to deal with unobservable confounding factors. A few include lagged dependent variables, that is, past values of the caseload.
Although the studies vary in the control variables they include, which in turn affects the quality of their results, they also differ in smaller ways. Some studies include measures of economic conditions beyond the unemployment rate. A few are based on monthly rather than annual data. Some of the studies based on aggregate data define the caseload as the number of persons on aid divided by the population, whereas others use the number of cases divided by the population. Some use the entire state’s population as the denominator, whereas others use the population of women within certain age ranges. Estimates from the studies of reform as a bundle, which we cover in Section 4.3.3 below, suggest that such differences in detail have little impact on the estimated effects of reform.
Six studies depart from this pattern to an extent sufficient to warrant separate attention. Three focus on welfare transition rates. Hofferth, Stanhope, and Harris (2000a, 2000b) use individual-level longitudinal data from the PSID to estimate the effects of a number of specific reforms on rates of entry to and exit from welfare. Mueser et al. (2000) use administrative data to estimate the effect of reform as a bundle on entry and exit rates in five cities.
While most of the other studies analyze the level of welfare use over a period of several years, two studies analyze the change in the welfare caseload over a single time interval. Rector and Youssef (1999) use administrative data to analyze the percent decline in state-level caseloads (recorded as a positive number) between January 1997 and January 1998. MaCurdy, Mancuso, and O’Brien-Strain (2000) also use administrative data, focusing on the percent change in state-level caseloads between August 1996 and March 1999. Mead (2001) focuses on the percent change in state-level caseloads between 1994 and 1998. Unlike most of the other studies we review, none of these studies includes explicit controls for unobservable confounding factors. However, by focusing on changes in the caseload, rather than levels, they may partially control for such factors implicitly.35
Most of the aggregate studies use the logarithm of the annual state-level caseload as their dependent variable. For these specifications, the coefficients from the regression models are interpreted as the percent change in the caseload associated with a one-unit change in the explanatory variable. Thus, the coefficient on a welfare-reform dummy is interpreted as the percent change in the caseload associated with the reform. Estimates from the studies that analyze percent changes in the caseload are interpreted the same way. In the survey-based studies, the dependent variable indicates whether the family was on welfare over some time period. The coefficients from these models are interpreted as the percentage-point change in welfare use associated with a unit change in the regressors, similar to the impact estimates from the random assignment studies. To aid in comparing the two types of estimates, we report the corresponding percent changes for all estimates in column (12) of Tables 4.2 and 4.3.36
Finally, since most econometric studies present more than one estimate of the effects of reform, we attempt to include in Table 4.2 the results from the authors’ preferred specifications. In a few cases, we have included estimates from other specifications as well, when those additional estimates add important insights into the effects of a particular reform or reform bundle. In a couple of cases, we were unable to determine which specification the author(s) preferred. In those cases, we included estimates from what we considered to be the highest-quality specification.
4.3.2. Effects of Specific Reforms
We first consider econometric estimates of the effects of specific reforms. By the criteria described in Chapter 3, some of these estimates are of low quality, since they are based on regression models that fail to control for unobservable confounding factors. Most fall into the moderate quality category. These studies include controls for unobservable confounding factors but rely solely on dummy (or modified dummy) variables to capture the effects of specific reform policies. Thus, they utilize only temporal variation in policy to estimate the effects of the policy. Only a few studies employ both controls for unobservables and policy measures that capture additional dimensions of policy variation, thus providing high-quality evidence on the effects of specific reforms. However, even high-quality studies may suffer from power problems of the type discussed in Chapter 3.
Financial Work Incentives
Panel A of Table 4.2 presents estimates of the effects of financial work incentives. Of the six estimates, four accord with the prediction from the standard economic model described in Chapter 2. Estimates from the Council of Economic Advisors (CEA) (1997), Ziliak et al. (2000), and CEA (1999) show that incentives increase welfare use. The estimate from CEA (1999), which is based on a measure that captures the generosity of each state’s financial incentive, and thereby counts as high-quality evidence, is significant. Hofferth, Stanhope, and Harris (2000a, 2000b) estimate financial work incentives to decrease the exit rate from welfare, but to have no effect on reentry rates.
Work-Related Activities
Five studies attempt to estimate the effects of more stringent age exemptions from states’ mandates to engage in work-related activities. The results are presented in Panel B1 of Table 4.2. Only the coefficients from Rector and Youssef (1999) and the exit study by Hofferth, Stanhope, and Harris (2000b) have the expected sign. The other estimates are insignificant and indicate that stricter exemptions work to increase caseloads rather than to decrease them. As for the effects of more stringent deadlines for satisfying work-related activity mandates, presented in Panel B2, only one estimate is significant.
The studies are more consistent about the effects of increased sanctions. Six of the nine studies listed in Panel B3 report significant estimates that indicate that stiffer sanctions reduce the caseload. CEA (1999) provides high-quality evidence, employing a specification that both provides explicit controls for unobservables and allows the effects of sanctions to vary with their severity. Its estimates are negative and significant and indicate that the stiffest sanctions have the greatest effects on welfare use. Indeed, the estimated effects of full-family sanctions are very large, indicating that they reduce welfare use by 39 percent.
Rector and Youssef (1999) and MaCurdy, Mancuso, and O’Brien-Strain (2000) employ a similar set of policy measures. Their results are qualitatively similar to those from CEA (1999), although the magnitudes of their estimates are smaller.
Interpreting the magnitudes of these estimates warrants some caution. In other analyses not shown here, MaCurdy, Mancuso, and O’Brien-Strain (2000) regress changes in state-level caseloads between 1989 and 1992 on policy changes implemented between 1992 and 1996. Since policy changes made after 1992 logically cannot affect behavior prior to 1992, these regressions shed some light on the policy endogeneity problem, that is, on the extent to which behavior influenced policy, rather than the other way around. The coefficient on the full-family sanctions dummy is statistically significant and, interpreted at face value, suggests that sanctions reduced pre-reform caseloads by 18 percent. Since no states implemented waivers involving full-family sanctions until late in 1994 (CEA, 1999), this effect clearly cannot be attributed to sanction policy. Rather, it may be evidence of policy endogeneity, indicating that states with large (percentage) reductions in their caseload during the pre-waiver period were more likely to seek waivers for full-family sanctions. Alternatively, it may reflect the effects of some other policy change that typically preceded the sanctions in states that eventually received sanction waivers.
Time Limits
Eleven studies address the effects of time limits. All can be interpreted as at least implicitly estimating the behavioral effects of time limits, rather than their mechanical effects, because the sample periods analyzed generally ended before recipients began exhausting their benefits. All but one of the estimates suggest that time limits reduce welfare use. However, of the studies based on aggregate data, only the estimate from CEA (1997) is significant, and then only at the 10 percent level. The estimates from Hofferth, Stanhope, and Harris (2000a, 2000b) are insignificant as well.
Grogger and Michalopoulos (forthcoming) provide explicit estimates of the behavioral effects of time limits based on a reanalysis of data from Florida’s FTP program. Their analysis is structured around a theoretical model that predicts that families with the youngest children should reduce their welfare use the most once time limits are imposed. The reason is that such families have the longest period over which to spread their limited benefits, and thus the greatest incentive to save their benefits for future use.
The estimate reported in Panel C of Table 4.2 is the coefficient on an interaction term between the FTP treatment group dummy and a function of the age of the youngest child in the family.37 The coefficient is statistically significant and suggests that the time limit component of FTP indeed reduced welfare use in a manner that was greatest for families with the youngest children.
In three complementary studies, Grogger (2000, 2002, forthcoming) estimates the effects of time limits using family-level data from the CPS and the SIPP. He reports that, for families whose youngest child is less than 13, time limits reduce welfare use by the most among the families with the youngest children.38 For families whose youngest child is over 13, many of which will become ineligible before they could reach the federal five-year limit, time limits have no significant effect.
Family Caps
Six studies estimate the effects of family caps using modified dummy variables. Two of the coefficients in Panel D are significant. They are mixed in sign, however, providing little reliable guidance as to the effects of this important policy reform on welfare use.
Child Support Enforcement
Two studies consider the effects of child support enforcement using variables that reflect the extent of child support payments to families on welfare. Huang et al. (2000) provide high-quality evidence, including using state and year dummies in the regression model and measuring the effects of policy changes via the average payment to welfare families in each state and year. Their estimate is highly significant and suggests that higher child support payments substantially reduce welfare use. Mead (2000) employs a similar policy measure and obtains similar results.
4.3.3. Effects of Reform as a Bundle
Over a dozen studies have attempted to estimate the effects of welfare reform as a bundle. All of these studies characterize reform using modified dummy variables. Some distinguish the effects of waivers from the effects of TANF. The results are presented in Table 4.3.
Of the nine sets of estimates that are based on administrative data and reported in Panel A of Table 4.3, seven indicate that the introduction of any (statewide) waiver reduced the caseload. These estimates range from —1.5 percent to —13.8 percent. The lowest estimate is from Levine and Whitmore (1998) and comes from a model that also controls for stricter sanctions. It should be interpreted as the effect of reform policies other than stricter sanctions and, thus, is not directly comparable to the estimates from the other studies. The two studies that estimate the effects of TANF report even larger effects, ranging from —18.8 to —34.7 percent. Most of these estimates are significant and all suggest that reform, under both waivers and TANF, has reduced welfare caseloads.39
Four sets of authors provide results from the March CPS. Grogger (2000) and O’Neill and Hill (2001) analyze data from single mothers, who are the primary recipients of cash aid. They analyze individual-level data on welfare use, using a dummy dependent variable that is equal to one for women who report welfare use in the previous year.
Moffitt (1999) and Schoeni and Blank (2000) focus on women between the ages of 15 and 54. They first aggregate the data into cells defined by state of residence, year, age, and education. These cells constitute their units of observation. Their dependent variable is the rate of welfare use within each of the cells (not the logarithm of that rate). These authors estimate separate models by different levels of education. This allows us to see whether the estimated effects of reform are concentrated primarily among the poorly educated, who make disproportionate use of the welfare system. If instead the estimated effects of welfare reform were similar across all levels of education, we would be concerned that the estimates did not truly reflect the effects of reform, but rather of some unobservable confounding factor.
Moffitt analyzes the effect of waivers on welfare use; Grogger analyzes the effect of reform, defined by the presence of either a statewide waiver or a TANF plan; and Schoeni and Blank and O’Neill and Hill consider the effects of waivers and TANF separately. All use the unemployment rate to control for the state of the economy, each states’ maximum welfare benefit, and a set of variables to control for maternal education and age. O’Neill and Hill control for wages as well. Grogger and O’Neill and Hill also control for family size, race, and the age of the youngest child in the family. All the models control for state fixed-effects. Most use year dummies to control for general trends in welfare use. O’Neill and Hill are the exceptions, using more restrictive linear and quadratic terms in time, instead.
Of the estimates from Moffitt, Grogger, and O’Neill and Hill, all but one are negative and significant. In relative terms, they indicate that welfare reform reduced welfare use by 2 to 20 percent, which is within the range of estimates from the studies based on administrative caseloads. O’Neill and Hill report that TANF has larger effects than waivers, echoing the results from CEA (1999) and Wallace and Blank (1999).
As noted above, Moffitt and Schoeni and Blank report separate results for groups defined by their level of education, which are presented in Panel B2 of Table 4.3. Regarding the effects of waivers, both sets of authors find that welfare reform has its largest effects on high school dropouts and smaller effects on women who attended college. In both studies, only the effects for dropouts are statistically significant. Schoeni and Blank find TANF to have larger effects than waivers, which is consistent with the evidence from other authors. Their estimates for dropouts and high school graduates are significant, whereas their estimate for women with higher education is positive though insignificant.
Panel C of Table 4.3 reports results from a study of welfare dynamics, that is, of entries and exits from the welfare rolls. Mueser et al. (2000) find that reform has affected both types of welfare transitions, although the effects vary by the type of reform. Waivers have small and insignificant effects on welfare entries, whereas TANF reduced welfare entries significantly. Both types of reforms increase welfare exits significantly, but the effects of waivers are stronger.
Although the majority of the evidence presented in Table 4.3 is consistent with the notion that reform as a bundle reduced welfare use, two studies suggest that it may have actually raised welfare use, albeit with an insignificant positive effect (Figlio and Ziliak, 1999; Bartik and Eberts, 1999). Beyond their conclusions, these two outliers differ from the other studies by including lagged dependent variables (that is, past values of the welfare caseload) as explanatory variables in their regression models. In the jargon of econometrics, models that include lagged dependent variables are referred to as dynamic, whereas models without them are referred to as static. The authors argue that such dynamic models are necessary to capture potentially sluggish adjustment of caseloads to changes in policy and economic conditions. According to Figlio and Ziliak (1999), it is the presence of the lagged dependent variables, more than any other reason, that explains the difference in results between the static and dynamic models.
For understanding the effects of welfare reform, this raises two important questions. First, why do the lagged dependent variables make such a difference? Second, which set of estimates is correct, if either?
Adding lagged dependent variables to a model raises a number of technical issues that do not arise in the context of static models. First, state fixed-effects models are inconsistent in the presence of lagged dependent variables. Although Ziliak et al. (2000) choose an alternative approach to deal with the unobserved heterogeneity problem, that method (known as first-differencing) may also yield inconsistent estimates in the presence of lagged dependent variables (Nickell, 1981).40
Furthermore, adding lagged dependent variables to the model exacerbates an already difficult collinearity problem. From inspecting Figure 4.1, it is easy to see that lagged values of the caseload are highly correlated with both the unemployment rate and the adoption of state welfare reforms, both of which are already highly correlated with each other. Adding lagged dependent variables to the model thus turns the difficult problem of distinguishing the effects of welfare reform from the effects of the economy into the even more difficult problem of distinguishing the effects of welfare reform from the effects of the economy and from recent trends in the caseload itself.
Such an undertaking might nevertheless be worthwhile if, in the end, we were left with a model that provided a deeper understanding of welfare dynamics and the effects of policy on the behavior of welfare recipients. However, recent work suggests that adding lagged dependent variables to an otherwise static regression model is unlikely to yield such an understanding. This insight stems from a recent study that analyzes the relationship between the nominally dynamic regression models that appear in the caseload literature and true welfare dynamics (Klerman and Haider, 2000).
In the welfare setting, dynamics refer to "flows," that is, to transitions on and off the welfare rolls by welfare entrants and welfare leavers. With information on those flows, we can compute the "stocks," that is, the caseload, at any point in time. With information on how policy affects those flows, we can compute how policy affects the stocks, both instantaneously and over time. Clearly, such information would serve a number of important purposes.
In the sense of Figlio and Ziliak (1999) and Bartik and Eberts (1999), however, the notion of dynamics refers not to welfare transitions and how welfare flows affect welfare stocks, but rather to how past welfare stocks are correlated with current welfare stocks. A key question is thus whether correlations among past and current stocks provide even indirect information about welfare transitions. Klerman and Haider (2000) address this question and provide a number of conditions under which nominally dynamic regression models, that is, those that include lagged values of the caseload as regressors, provide information on welfare dynamics. The conditions are highly restrictive. One condition requires welfare exit rates to be independent of the amount of time that the recipient has already spent on welfare. A substantial body of empirical evidence points to the contrary, indicating that exit rates fall as the spell length increases (Blank, 1989; Bane and Ellwood, 1994).
As a result, the nominally dynamic models of Figlio and Ziliak (1999) and Bartik and Eberts (1999) are unlikely to provide even indirect information about the effects of welfare reform on welfare dynamics. Of course, the same can be said about the static models: None of them addresses the issue of welfare dynamics at all. At the same time, however, the technical issues associated with consistently estimating static models are less difficult than those associated with the nominally dynamic models, and, in addition, the collinearity issues that confront the static models, while considerable, are less daunting than those confronting the nominally dynamic models.
Moreover, the results from the more disaggregated studies of welfare reform also suggest that reform has affected welfare use. The studies of Moffitt and Schoeni and Blank find that the effects of reform are concentrated among women with low levels of education, which increases our confidence that the results are "real," and not merely the result of unobserved confounding factors. Put differently, if they had found that welfare reform affected college women to the same extent that it affects dropouts, they would have cast doubt on all the prior studies. However, because they found the effects to be strongest among dropouts, they increase our confidence that the estimates reflect the effects of reform, rather than unobservable confounding influences. Perhaps more importantly, direct evidence on welfare dynamics indicates that welfare reform affects entries and exits in plausible ways (Mueser et al., 2000; Hofferth, Stanhope, and Harris, 2000a, 2000b).
A further piece of evidence also suggests that the lagged dependent variable models understate the effects of reform. Ziliak et al. (2000) use nominally dynamic models to estimate the effects of a number of specific policy reforms, including work-related activity mandates. Their estimate, which appears in Panel B2 of Table 4.2, indicates that work-related activity mandates have a very small effect on the caseload.41 This contrasts with the results from the 13 random assignment studies that focused on work-related activity mandates, 12 of which produced significant decreases in welfare use.
Finally, beyond the narrow question of whether nominally dynamic econometric models understate the effects of welfare reform, there is the more general question of whether welfare reform contributed to the unprecedented decline in welfare use that took place during the 1990s. On this more general question, further evidence can be brought to bear. In the next chapter, we show that almost all of the random assignment experiments increased employment. The few econometric studies on the topic concur that reform increased work among welfare-prone populations.
This is not altogether surprising, since all the major policy reforms would be expected to increase employment. Although different reforms have different incentives for welfare use, all the major reforms provide positive incentives for work. Nevertheless, this observation makes an important point: The major welfare reforms implemented during the 1990s affected behavior. Given that they affected behavior, the only logical argument that we could make to support the contention that they did not affect welfare use is that, on a nationwide basis, the conflicting incentives resulting from the different reforms exactly cancelled each other out.
The results from Table 4.1 show that, in individual cases, such "policy canceling" can occur. Nevertheless, it seems unlikely to have occurred on a nationwide basis. The reason is that the financial work incentives implemented in MFIP, FTP, and Jobs First, which provide perhaps the strongest evidence of policy canceling, were among the most generous in the country. Nationwide, although 36 states had implemented some sort of financial incentive by 1997, 37 had implemented work-related activity mandates that were more demanding than AFDC/JOBS, all but two had implemented more stringent sanctions for noncompliance, and all but three had implemented time limits.42 Of course, most states implemented several such polices in combination. From a purely numerical perspective, it seems unlikely that the typical financial incentive could have completely offset the combined effects of work-related activity mandates, sanctions, and time limits, each of which appears to have reduced welfare use.
For all these reasons, as well as the direct evidence provided by most of the econometric studies, we conclude that welfare reform played an important role in reducing the welfare caseload during the late 1990s. This is not meant to deny the importance of other factors. The economy played an important role, and as several analysts have suggested, it may have been the single most important explanation for why caseloads fell. However, despite a few studies that make claims to the contrary, the bulk of the evidence suggests that welfare reform made an important contribution.
4.4. EVALUATING THE EFFECTS OF WELFARE REFORM ON WELFARE USE
Having presented the results of several studies, in this section we attempt to synthesize them to convey what is known about the effects of welfare reform on welfare use. We consider the random assignment and econometric studies together, weighing both the quantity and quality of the evidence. We begin by discussing the effects of specific reforms and then turn to discussing their effects as a bundle.
4.4.1. Effects of Specific Reforms
Financial Work Incentives
The effects of financial work incentives are the primary focus of three high-quality random assignment studies and six econometric studies, only one of which rates as high-quality by the criteria discussed in Chapter 3. Estimates from MFIP-IO and the high-quality econometric study (CEA, 1999) indicate that stronger financial work incentives are associated with higher rates of welfare use, as the standard economic model would predict. The CWPDP and WRP-IO programs had no significant effect on welfare use, but their financial work incentives were fairly weak. Estimates from all but one of the lower-quality econometric analyses are insignificant.
The programs that combine financial work incentives and mandated work-related activities also shed some light on the effects of the incentives. Since the financial incentive should increase welfare use, all else equal, whereas the work-related activity mandate should decrease it, the net effect of such programs is ambiguous. Of the four random assignment studies that combine these two reforms, those with stronger financial work incentives tend to generate positive net effects on welfare use, while those generating insignificant or negative effects involved relatively weak financial incentives.
Evidence from the three SSP programs, which tied financial incentives to hours of work, is consistent with this pattern as well. Those programs provided strong financial work incentives in the form of earnings supplements for consumers who satisfied the programs’ work requirements. Those programs substantially increased the rate at which consumers received transfer payments.43
Mandatory Work-Related Activities
Mandatory work-related activities have received a substantial amount of study, both from random assignment and econometric analyses. As a result, certain conclusions about these policies can be drawn fairly strongly. Of the 13 random assignment studies that focus on work mandates, 12 generated significant declines in welfare use during the first two years after random assignment. Programs with stronger enforcement generally had larger effects. The programs stressing job search generally yielded greater decreases than the programs stressing skills development, but the mean difference was relatively small, and the contrast involved only four search-oriented programs. The impacts of both types of programs faded over time.
Much less can be said about other aspects of states’ work-related activity mandates. Among the several econometric studies that analyze age-exemption thresholds or shorter deadlines for satisfying the mandates, the conclusions are quite mixed. Only one of these studies satisfies our criteria for providing high-quality evidence, and it yields the perverse (though generally insignificant) result that more stringent exemption criteria increase the caseload.
Nine studies estimate the effect of sanctions for noncompliance with the work mandates. Seven report that sanctions significantly reduce welfare use. Three studies report that stricter sanctions have greater effects than weaker sanctions. However, the interpretation of those estimates is clouded by results suggesting that sanction policies implemented after 1994 reduced caseloads between 1989 and 1992. Moreover, none of the studies estimates the effects of the monetary value of sanctions, and none incorporates any information about the frequency with which sanctions are actually imposed.
Time Limits
Of the seven moderate-quality econometric studies that implicitly estimate the behavioral effects of time limits, most suggest that time limits reduce welfare use, although only one is even marginally significant. Four high-quality econometric studies, two of which are very similar, find that time limits reduce welfare use the most among families with the youngest children. This suggests that time limits have behavioral effects, because the families that reduce their current welfare use the most are those with the most to lose by prematurely exhausting their benefits. However, all these studies rely on a number of assumptions to isolate the effects of time limits from the effects of other reforms.
Only two studies provide evidence on the mechanical effects of time limits. Evidence from both FTP and Jobs First suggests that welfare use falls considerably as families begin to exhaust their benefits.
Family Caps
Family caps have been the subject of six econometric studies, none of which provide high-quality evidence on their effects. Their results are mixed, providing little insight into the question of whether family caps have any effect on current welfare use.
Child Support Enforcement
Two econometric studies, including one that provides high-quality evidence, estimate the effects of child support enforcement on welfare caseloads. Both estimate that child support enforcement has substantially reduced the rolls.
4.4.2. The Effects of Reform as a Bundle
Six random assignment studies involve TANF-like bundles of reforms. Of those, four suggest that reform as a bundle reduced welfare use. Three of the programs showing the smallest reductions had time limits that were poorly understood by participants. If they had been better understood, the programs probably would have reduced welfare use more. The only program to raise welfare use prior to time limits becoming binding was Jobs First, which included an extraordinarily generous financial incentive.
In addition, over a dozen econometric studies have attempted to estimate the effects of reform as a bundle on aggregate welfare use. Except for a few analyses that use lagged values of the caseload as controls for current caseloads, these studies generally find that reform has reduced the welfare rolls. For the reasons we detail above, we place relatively little weight on the studies that employ lagged caseloads.
Because we view the lagged-caseload studies less favorably than Bell (2001), who recently reviewed much of the econometric literature on the caseload decline, it is worthwhile to explain why our conclusions differ. First, Bell is more optimistic than we are that the lagged-caseload models provide a reasonable approximation to the process of welfare entry and exit that must underlie any change in the caseload. Although we agree with Bell about the importance of analyzing such welfare transitions directly, our reading of recent research suggests that lagged-caseload models are unlikely to provide insights into the process driving entries and exits (Klerman and Haider, 2000).
Beyond this technical difference of opinions, however, we think there is a further reason why our conclusions differ: We consider a broader range of evidence. Bell did not review either of the studies that analyze welfare transitions directly. Moreover, he limited his review to econometric studies. By considering the results from Mueser et al. (2000) and Hofferth, Stanhope, and Harris (2000a, 2000b), we see that the indirect evidence on welfare dynamics from the lagged-caseload studies often contradicts the direct evidence from the welfare-transitions studies. By considering the random assignment studies, we see that the lagged-caseload results regarding the effects of specific policy reforms often contradict the results from high-quality experiments. In our view, this additional evidence is persuasive.
Estimates from the other studies of reform as a bundle generally suggest that reform has played an important role in reducing the caseload. However, precise estimates vary widely. The estimated reductions attributable to waivers range from 12 to 31 percent. The three studies that attempt to distinguish the effects of TANF from the effects of waivers generally find TANF to have even larger effects.
At the same time, nearly all the econometric studies agree that the economy played an important role in reducing the caseload.44 Most of the analyses suggest that the economy accounted for one-fourth to one-half of the 1993—1996 decline in the welfare rolls. The few analysts who consider the post-PRWORA period explicitly generally credit the economy with a smaller fraction of the caseload decline over that period, which is consistent with the fact that the decline in the unemployment rate slowed during the late 1990s. Other social policy changes had important effects as well, with one estimate suggesting that the changes to the EITC explained 16 percent of the decline in welfare use (Grogger, forthcoming). Welfare reform appears to have played an important role in reducing the caseload, but it was hardly the only factor underlying the unprecedented declines of the mid- to late-1990s.
4.5. CONCLUSIONS
Many of the effects of welfare reform on welfare use have been well-studied. Over a dozen econometric studies have attempted to estimate the effects of reform as a bundle, and all but a few report that reform had substantial effects on the caseload. Moreover, as we explain above, the contradictory evidence comes from a small number of studies that employ a technique that poses considerable technical challenges. All but one of the econometric studies concur that the economy played an important role in reducing caseloads during the 1990s. Regardless of how effective welfare reform might have been, in the absence of the booming labor market, the decline in welfare use would have been substantially smaller.
In terms of the effects of specific reforms, over a dozen experimental studies have focused on mandatory work-related activities, and most find that such policies reduce welfare use by a significant and substantial amount. The few that find otherwise generally involved weakly enforced mandates or included a generous financial incentive along with the work mandate.
Beyond work-related activity mandates, however, evidence on the effects of specific reforms becomes thinner. Evidence on the effects of financial work incentives is consistent with the notion that substantially increasing the generosity of financial work incentives increases welfare use. Much of the evidence for this conclusion is inferred from programs that combined financial work incentives with mandatory work-related requirements. Only four high-quality studies focus directly on financial work incentives.
Sanctions for noncompliance with mandated activities have been the focus of substantial policy interest. Several studies find that stricter sanctions lead to a greater reduction in the caseload, but some of that reduction may have preceded the implementation of the sanctions. None of the studies to date attempts to monetize the effects of sanctions, which may be important since a full-family sanction in a low-benefit state may actually cost the family less than a partial sanction in a high-benefit state. Even more troubling is the fact that no study has estimated how the frequency of sanctions affects welfare use. States vary widely in the extent to which they actually impose sanctions, and deterrence theory (Becker, 1968) suggests that moderate sanctions imposed with a high frequency may be as effective as severe sanctions that are seldom imposed.
Similarly, there have been relatively few high-quality studies of the effects of time limits. Four econometric studies (two of which are quite similar) show that time limits have greater effects on families with younger children. This suggests that time limits have behavioral effects, since it suggests that families that have more to lose by prematurely reaching the limit are more likely to reduce their current welfare use. Two random assignment studies show sharp declines in welfare use starting at the time when families begin to exhaust their benefits. The importance of such mechanical effects is likely to grow in the near future, as increasing numbers of recipients reach the five-year limit on federal funding.
After time limits, the number of studies providing impacts for specific policy reforms gets even smaller. There is one high-quality study on the effects of age exemptions for mandatory work-related activities and one on the effects of child support enforcement. There are none on the effects of family caps.
In summary, if we think about the welfare column of our policy-outcome matrix, a few cells are well-filled. There are a few more that contain evidence from a few high-quality studies. The fact that these results generally accord with predictions from the standard economic model gives us more confidence in them than we would have based on their numbers alone. However, many of the rows are nearly empty, including some that involve important policy reforms.
30 More detailed subgroup-specific impacts are presented in Appendix A.(back)
31 Members of the treatment groups were subject to some other policy changes as well, such as extended transitional child care or a food stamp cash-out. Because the MFIP treatment group received its food stamp benefits in the form of cash, the MFIP welfare use measure is an indicator of whether the participant received cash aid (welfare plus cashed-out food stamp benefits) in the case of the treatment group, or whether the participant received cash aid (welfare) or food stamps benefits in the case of the control group. For both groups, the welfare use indicator also reflects receipt of General Assistance.(back)
32 In principle, this could be because of the control-group crossover that occurred during years 4 and 5, when control group members were allowed to participate in the welfare-to-work programs that were previously available only to members of the treatment group. However, Hamilton et al. (2001) provide evidence that there was little actual crossover, suggesting that crossover had little to do with the program fade-out.(back)
33 In principle, we could use the site- and quarter-specific estimates provided in Gordon and Agodini (1999) to compute impact estimates over the post-VIEW period for the three sites that implemented VIEW prior to the end of the sample period. For a number of reasons, we do not take this approach. First, the follow-up periods are short for two of the three sites. Second, it is not possible for us to construct standard errors for such estimates. Third, the site with the largest post-VIEW impacts also had large pre-VIEW differences between the treatment and control groups, raising questions of whether randomization was properly conducted at that site.(back)
34 Treatment group members who were deemed to be particularly disadvantaged received a 36-month time limit.(back)
35 Differencing the data within each state provides an alternative to the state-fixed effects approach for controlling for state-specific unobservables. However, the approach requires that both the dependent and independent variables be differenced, whereas these studies difference only the dependent variable and, in some cases, a few of the independent variables.(back)
36 Unfortunately, Hofferth, Stanhope, and Harris (2000a, 2000b) do not provide enough information for us to transform their estimates in this way.(back)
37 The function is given by age* = (Age of the youngest child Ð 14) for families with three-year time limits and youngest children less than 15 and by age* = (Age of the youngest child Ð 15) for families with two-year time limits and youngest children less than 15. For families with older youngest children, age* = 0, since such families will become ineligible when their youngest child turns 18, which will take place before they could possibly exhaust their benefits.(back)
38 In these studies, age** = (Age of the youngest child Ð 13) for families with youngest children less than 13. For families with older youngest children, age** = 0.(back)
39 Wallace and Blank (1999) note that many of these models fail to track pre-PRWORA caseload trends very well.(back)
40 Ziliak et al. (2000) claim that their sample period is long enough to avoid these problems, but they provide no direct evidence to support their claim.(back)
41 Moreover, only two of the five coefficients that contribute to the estimate in Table 4.2 were both negative and significant.(back)
42 These figures are based on the authors' tabulations of data from CEA (1999).(back)
43 New Hope may appear to be an exception to this general rule, since it provided a strong financial incentive but did not raise AFDC use. However, for programs such as New Hope, the economic model predicts an increase in the rate of transfer payments, that is, in receipt of the earnings supplement. Unfortunately, Bos et al. (1999) do not provide impact estimates for receipt of the earnings supplement that are comparable to the impact estimates for AFDC.(back)
| Table of Contents | Previous | Next |