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Rebecca M. Blank

Working Paper 8983

1050 Massachusetts Avenue
Cambridge, MA 02138
June 2002

This paper was commissioned by the Journal of Economic Literature . Thanks are due to Lucie Schmidt and
to Elizabeth Scott for excellent research assistance, and to Jeffrey Grogger, Charles Michalopoulos, Robert
Moffitt and an anonymous referee for comments and advice. The views expressed herein are those of the
author and not necessarily those of the National Bureau of Economic Research.

© 2002 by Rebecca M. Blank. All rights reserved. Short sections of text, not to exceed two paragraphs, may
be quoted without explicit permission provided that full credit, including © notice, is given to the source.

Evaluating Welfare Reform in the United States
Rebecca M. Blank
NBER Working Paper No. 8983
June 2002

This paper reviews the economics literature on welfare reform over the 1990s. A brief summary
of the policy changes over this period is followed by a discussion of the methodological techniques
utilized to analyze the effects of these changes on outcomes. The paper then critically reviews the
econometric and experimental literature on caseload changes, labor force changes, poverty and income
changes, and family formation changes. A growing body of evidence suggests that the recent policy
changes have influenced economic behavior and well-being in a variety of ways. One particular set of
“new-style” welfare programs seems to show especially promising results, with significantly increased
work and earnings and reduced poverty.

Rebecca M. Blank
Gerald R. Ford School of Public Policy
440 Lorch Hall
611 Tappan Street
University of Michigan
Ann Arbor, MI 48109-1220
and NBER
Tel: 734-763-2258
Fax: 734-763-9181


Over the 1990s the United States fundamentally changed the structure of its
public assistance programs to low-income families. These policy changes have, in turn,
generated a growing body of economic research that has evaluated their effects. This
article reviews the major changes in U.S. welfare programs over the 1990s and critiques
some of the key methodological approaches and results in areas where a substantial
economic research literature has accumulated. I particularly focus on areas where the
new research contributes to long-standing debates.
It is worth noting that the U.S. policy changes have been much discussed in other
countries and the evaluation literature from the U.S. may be increasingly relevant to
policy debates elsewhere. For instance, in 1996, Canada gave provinces greater
discretion over their social assistance programs, similar to changes the U.S. As we shall
discuss below, Canada enacted a very interesting demonstration program in the 1990s
(the Self Sufficiency Project), designed to move women on welfare into work. In 1999,
Great Britain enacted the Working Families Tax Credit, a generous tax credit for lowincome working families, similar to the U.S. Earned Income Tax Credit program. Some
communities in Germany are imposing time limits on the receipt of public assistance
(Feist and Schöb, 1998). In contrast to earlier decades, when the different design and
lower generosity of U.S. social welfare programs led U.S. policies to be dismissed as
irrelevant or aberrant by other westernized nations, during the 1990s many of these
countries watched the U.S. welfare experiments with great interest.1


Not discussed here are social insurance programs such as Social Security or Unemployment Insurance,
around which there has also been a great deal of trans-Atlantic conversation.


I. Federal Changes in U.S. Welfare Programs Over the 1990s
The U.S. enacted major welfare reform legislation in August, 1996. The Personal
Responsibility and Work Opportunity Reconciliation Act (PRWORA) passed with a
relatively high degree of bipartisan support. President Bill Clinton had, however, vetoed
two earlier versions of this bill and it remained controversial. Several of his senior
advisors resigned in protest when he signed PRWORA into law.2
The major provisions of PRWORA included:

Devolution of greater program authority to the states. PRWORA replaced the
federal Aid to Families with Dependent Children Program (AFDC) – the primary
cash assistance program for low-income families -- with the Temporary Assistance
for Needy Families (TANF) block grant. This essentially removed almost all federal
eligibility and payment rules, giving states much greater discretion in designing their
own cash public assistance programs. This also eliminated a federal entitlement to
cash assistance. States could choose which families they supported.


Changes in financing. TANF replaced a matching fund arrangement under AFDC, in
which federal funding moved up or down with state funding. The TANF block grant
was fixed and the contribution for each state was determined by the federal AFDC
matching grant contribution in the years prior to PRWORA. States were required to
maintain at least 75 percent of their previous state spending levels on AFDC in order
to receive the full block grant.3


Ongoing work requirements. By 2002, at least 50 percent of all recipient families and
90 percent of two-parent families were required to be working or in work preparation
programs, although states were given great discretion to design and implement these
programs. The law treated caseload reductions as similar to work, however. Thus, a
state which reduced its caseload by 50 percent would meet its work requirement,
regardless of how many current or former recipients were actually employed.


Incentives to reduce non-marital births. There was more rhetoric than program in the
legislation in this area, but three of the four stated goals of PRWORA involved
reducing non-marital births and encouraging marriage. States that reduced out-ofwedlock child bearing without raising abortion rates qualified for special bonuses.


For a detailed description of the events leading up to this legislation, see Weaver (2000). For further
discussion about the provisions of PRWORA see Blank (1997b) or Blank and Ellwood (2002). Moffitt
(1999b) discusses the factors behind PRWORA’s passage. Moffitt (forthcoming) provides a more detailed
summary of the changes from AFDC to TANF.
Not included in this paper is any discussion of the public finance literature that investigates the potential
impact of block grants on welfare funding. For a good overview of these issues, see Chernick (1998).



Five year maximum time limit. PRWORA set a lifetime limit of 60 months on the
receipt of TANF-funded aid. States could exempt up to 20 percent of their caseload
from this limit, could set shorter time limits if they chose, or could continue funding
assistance to families entirely out of state funds after 60 months.

Although this paper will focus less on these issues, PRWORA also imposed additional
limits on eligibility for Food Stamps and Supplemental Security Income (SSI, the cash
assistance program to low-income aged and disabled individuals) among certain
populations. Legal immigrants who arrived after August 1996 were largely denied access
to TANF and to these other programs; the impact of this policy change will grow over
time as an increasing share of U.S. immigrants will have arrived post-PRWORA.
Finally, PRWORA made changes designed to encourage greater paternity establishment
and more payment of child support by absent parents.
While the 1996 legislation has received the most public attention, it was preceded
by a variety of earlier and significant changes. Growing dissatisfaction with AFDC had
led an increasing number of states to seek waivers from the AFDC rules. These waivers
were mostly designed to allow states to more stringently enforce work requirements for
welfare recipients. Such waivers had started under President Ronald Reagan, but the
Clinton Administration actively encouraged more expansive state-wide waiver programs.
As a result, by the time PRWORA passed, 27 states had major state-wide waivers in
place. Most of these states designed new TANF-funded welfare programs that were
closely based on their waiver experiments, although virtually all waiver states used their
new discretion under PRWORA to make additional program changes.
All of these waiver programs had to be seriously evaluated by the states that
implemented them. The Department of Health and Human Services (HHS), which


approved and administered the waivers, typically required some form of randomassignment evaluation. Over time, this generated a body of literature about welfare-towork programs that was crucial in convincing people that such programs could have
positive effects on earnings and labor supply and negative effects on welfare spending.
Along with reform of traditional cash welfare programs, there were also major changes in
federal legislation affecting low wage jobs and workers over the 1990s. The minimum
wage rose from $3.35 at the end of 1989 to $5.15 in 1997. By 2000, this left real
minimum wages 10.8 percent above their levels in 1989.
Even more important, one of the first legislative proposals from the Clinton
administration to receive Congressional approval in 1993 was a major expansion of the
Earned Income Tax Credit (EITC). The EITC operates as a refundable tax credit through
the federal tax system to subsidize low wage workers in low income families. Figure 1
describes the EITC subsidy as of 2000. Nonworkers receive no subsidy. Low income
low wage workers with one child (two or more children) are initially subsidized at a rate
of 34 percent (40 percent). Over some income range they receive a flat subsidy of $2353
($3888), and as their income increases further this is taxed away at a rate of 15.98 percent
(21.06 percent). This subsidy offsets federal income tax obligations (including taxes that
fund the Social Security and Medicaid programs) and results in subsidies (checks from
the government) for workers whose EITC subsidy is greater than their tax obligations.4
The combination of increased minimum wages and increased EITC subsidies
meant that the real earnings plus wage subsidy (in 2000 dollars) received by a woman
with one child working full time at the minimum wage rose from $10,568 in 1989 to


More detail on the EITC is available in U.S. House of Representatives (2000, p808-813). For a history of
the EITC, see Ventry (2000).


$12,653 in 2000, a 19.7 percent increase. For a similar woman with two or more
children, real earnings and subsidies rose from $10,568 in 1989 to $14,188 in 2000, a
34.3 percent increase. These changes should have greatly increased the work incentives
for low-wage single mothers with children.
Two other federal legislative changes also deserve mention. First, from the mid1980s on, access to public health insurance became increasingly delinked from
participation in cash public assistance programs. By 1999, all children in families whose
income was below 100 percent of the poverty line were eligible for Medicaid, the
publicly-funded health insurance program for low-income persons.5 In addition, women
who left welfare for work were eligible for one year of transitional Medicaid coverage.6
Because many eligible children did not appear to be accessing Medicaid, in 1997
Congress funded a $24 billion, 5-year program known as the Children’s Health Insurance
Program (CHIP), providing incentives and funding to states to expand health care usage
and health insurance access among low-income children.
There were also substantial changes in subsidies for child care assistance.
PRWORA abolished a plethora of older programs and created a single Child Care and
Development Block Grant. States were also allowed to use a certain share of their TANF
funds for child care. In addition, there were expansions in the Child Care Tax Credit for
lower middle income families.7


Since 1983, all pregnant women and children age 5 or less in families with incomes below 133 percent of
the Federal poverty line have access to Medicaid; 23 states use a higher cutoff point. Older children, born
after September 1983, in families below 100 percent of the poverty line are also covered by Medicaid; 26
states set a higher cutoff point for eligibility for these older children (Ku, Ullman and Almeida, 1999). For
more detail on Medicaid and how it operates, see Gruber (forthcoming).
Thirteen states extend this for more than one year.
Loprest, Schmidt and Witte (2000) discuss these changes in more detail. For a summary of the research
on the impacts of child care subsidies, see Blau (forthcoming) and Anderson and Levine (2000).


Combined, these changes constitute a revolution in public assistance programs
within the United States over this past decade. Federal dollars available to support
working low income families increased from $11.0 billion in 1988 to $66.7 billion in
1999.8 Dollars paid in cash welfare support to (largely nonworking) families headed by
non-elderly, non-disabled adults rose from $24 billion in 1988 to $27 billion in 1992,
then fell to $13 billion by 1999 (all numbers in 2000 dollars). This suggests that the work
incentives imbedded in the public assistance system should have increased markedly over
this period: cash assistance became far less available, welfare recipients were pushed
much harder to find employment and leave the rolls, the returns to low wage work rose,
and the availability of work supports (child care and health insurance) increased to low
income families.
Not unimportant, these changes took place at the same time as a major economic
boom. The U. S. unemployment rate fell to 5 percent in April, 1997, and remained at or
below this level until October 2001. Most places experienced worker shortages in the
years following the passage of the 1996 legislation, making employers more willing to
hire ex-welfare recipients. Wages among less skilled workers started to rise in 1995, for
the first time since the late 1970s (Blank and Schmidt, 2001). This meant that the
macroeconomy reinforced and supported the direction of legislative change over the
1990s. In many ways, the late 1990s were the best time imaginable to enact and
implement work-oriented welfare reform.


Blank and Ellwood (2002, Figure 1). This includes dollars spent on the EITC, child care assistance to
poor and near-poor families, and Medicaid and CHIP expenditures on low-income children and adults who
are not receiving cash assistance. It does not include money spent on job training or job placement
assistance, or cash benefits paid to working families.


II. The State Response
Describing the Federal changes provides only half of the picture. After the
passage of PRWORA each state began to design and enact its own TANF-funded
Historically, analysis of public assistance programs has focused on two
parameters: benefit levels and benefit reduction rates (BRRs). Figure 2 shows the income
available to a low-wage family under a typical welfare program. A maximum benefit
level, G, is available to non-workers. Workers earn an hourly wage rate w. As hours of
work (and earnings) increase, benefits are taxed away at a rate t (the BRR). Ongoing
historical discussion has focused on the trade-offs of higher benefits (raising G provides a
stronger safety net but discourages work and raises program costs) and higher BRRs
(raising t reduces the return to low levels of work but leads to lower program costs). The
Negative Income Tax experiments of the 1970s were largely experiments involving
different levels of G and t (Burtless, 1986; Ashenfelter and Plant, 1990).
Frustration with the work disincentives imbedded in traditional welfare programs
led President Reagan to promote welfare-to-work programs in the early 1980s.
Mandatory job search or job placement programs would replace the endless effort to
tinker with the contradictory incentives imbedded in a given level of G and t, by forcing
welfare recipients to work regardless of the resulting loss in benefit income. A strong
version of work requirements is a so-called “workfare” program, which mandates a
certain level of work in a publicly provided job as a condition of ongoing welfare receipt.
A less extreme requirement might mandate participation in a job preparation or job


For a description of the structure of means-tested programs prior to 1996, see Blank (1997a).


search program. A wide variety of states have experimented with different versions of
work requirements over the past 20 years.
Initially using waivers and later using their authority under PRWORA, states have
transformed the nature of public assistance programs. While benefit levels and BRRs
remain important parameters, states are increasingly using a wide variety of additional
program design components to promote work and to reduce caseloads. What follows is a
brief description of these changes. What will be clear is that both the number of possible
program parameters available to states has increased markedly, and that different states
are choosing very different combinations of these parameters. Hence, the variance across
states in their TANF-funded programs is enormous and still growing.
Benefit Levels. States have always been able to choose their own maximum
benefit levels for non-workers. This part of the system has changed little. Most states
over the 1990s made only small legislative changes in their benefit levels, even after the
passage of PRWORA. In fact, the overwhelming trend in benefit levels in the 1990s has
been inflation erosion in benefits (a trend visible since the early 1970s). Table 1 indicates
that the median benefit level (in $2000) fell from $480/month for a family of three to
$379 between 1990 and 2000. Most of this decline was due to inflation erosion. Similar
changes occurred across the distribution of benefit levels, as Table 1 indicates.10
As cash assistance becomes less broadly available, benefit levels are of decreasing
importance. The steady decline in benefit levels, however, should increase work
incentives over this period.
Benefit Reduction Rates. Under AFDC, BRRs were set by federal law (although a
few states received waivers to experiment with alternative BRRs in the early 1990s).


BRRs had been raised significantly in the early 1980s, and many AFDC recipients faced
almost 100 percent tax rates on their earnings.
A major change post-PRWORA is that many states have chosen lower BRRs, in
order to encourage work (and to a lesser extent, as a way of supplementing income
among low-wage workers). Free to set their own rules, many states have also chosen to
have BRRs rise at some point after a woman goes to work, so her public assistance
subsidy is reduced over time even if her earnings do not increase.
Table 2 is based on calculations of the cumulative cash welfare benefits available
over the first 24 months of work by a welfare recipient with two children whose earnings
are $6/hour (slightly above the minimum wage of $5.15 per hour) and who works parttime (30 hours/week) or full-time (40 hours/week). The first two columns show the
cumulative cash benefits that a welfare recipient family would have expected to receive
in each state in January 1996 (all numbers adjusted to 2000 dollars) if the mother went to
work under the old AFDC program. The second two columns show the cumulative cash
benefits that a family would have expected to receive in 2000 if the mother went to work
under each state’s TANF program.
The AFDC program provided little cash support to workers. Almost half the
states in 1995 would have paid no cash benefits to a part-time worker.11 Only 13 states
would have provided any support to a full-time worker.
By 2000, BRRs had fallen in almost all states, dramatically changing these
results. Almost all states provide some support to the mother who enters part-time work
in 2000; in 28 states this support exceeds $1000 over the first 24 months of work. Half

The standard deviation in benefits across states changed little over these 10 years.


the states also provide some cash supplement to the woman who enters full-time work,12
with the median state paying $299 in cumulative cash benefits over the first 24 months.
Sixteen states pay more than $1000 in benefits over these first 24 months.13
A change in the BRR is equivalent to a change in the effective wage rate (see
Figure 2). Because this imbeds both income and substitution effects, it is theoretically
ambiguous whether work incentives should rise or fall. Most labor economists assume
that substitution effects dominate income effects for low wage workers. This suggests
that lower BRRs should increase work incentives. Moffitt (1992) notes the remarkable
historical inelasticity of responsiveness among welfare recipients to changes in BRRs,
however, which suggests that the work incentive effect of lowering BRRs in the mid1990s might not be large. On the other hand, the changes in BRRs implemented in the
1990s were often made in conjunction with strong work requirements. As the discussion
of financial incentive programs in Section VIII below indicates, the combination of lower
BRRs and work mandates may have a quite powerful combined effect.
Note that lower BRRs may have other effects as well. In the presence of time
limits, lower BRRs keep welfare recipients on welfare longer and encourage families to
“use up” their time. If clients are aware of time limits and worried about using up their
public assistance eligibility, this will further increase their incentives to work and may
lead them to leave welfare even while still eligible for some benefits in order to preserve
future months’ welfare eligibility.

Differences across the states in columns 1 and 2 of Table 2 are entirely due to differences in AFDC
benefit maximums across states; all states are subject to identical (federally determined) BRRs.
Cumulative benefits equal 0 for a woman earning $6/hour if BRRs are very high (and in some states they
are 100 percent, so benefits are reduced $1 for $1 of earnings) and/or if benefit levels are very low (so that
one “works one’s way off welfare” more quickly).
More detailed information on these earnings disregard calculations are available from the author upon


Welfare-to-Work Programs. Virtually all states have tried to expand their
welfare-to-work programs starting in the early 1980s. Since the passage of PRWORA,
states are mandating participation in job search assistance and work preparation among a
much higher share of their caseload. By 1999 states reported that 38.3 percent of their
caseload was engaged in work or job activities, up from 20.4 percent in 1994.14
The exact meaning of “welfare-to-work” varies substantially across states. In the
early 1990s, many states ran both job placement and job training programs. By the late
1990s, the focus of most state programs was “work first”, aimed at getting recipients into
a job as soon as possible. Hence, most programs focus on narrow job preparation skills
(interviewing, getting along on the job, organizing child care) and job search assistance.
Relatively little money is currently being spent on longer-term training, a somewhat
controversial fact in many states.15
These work programs should increase work incentives, both by improving
employment-related skills and by establishing job search as an expected activity for
welfare recipients. Indeed, a number of states have focused on changing the “culture” of
their public assistance offices, retraining and reorganizing staff so that their primary goal
is to encourage work rather than to provide monthly assistance (Gais, et. al., 2001).
Sanctions. To enforce job search and work requirements, states have
implemented a variety of sanction policies aimed primarily at penalizing individuals who
do not respond to work requirements (most commonly, these are individuals who miss

The 1994 data is from U.S. House of Representatives (2000, Table 7-25). The 1999 data is from U.S.
DHHS (2000, Table 3:1).
See discussion of this issue by Strawn, Greenberg, and Savner (2001). Job training or education among
adults can be counted as a work activity, but cannot count toward the first 20 hours/week of required work
An exception is teen mothers under age 18, who are required to participate in education activities unless
they hold a high school degree.


required job preparation or job search sessions). Sanctions involve a reduction in welfare
benefits, but states vary in how much they reduce benefits and for how long. Pavetti and
Bloom (2001) classify 25 states as “strict”, including a number of states that impose
permanent full benefit losses on the families of noncompliant individuals. They classify
13 states as “lenient,” imposing only temporary and partial reductions.
If low BRRs are the “carrot” for participating in welfare-to-work programs
(providing ongoing subsidies to those who can only find low wage jobs), then sanctions
are the “stick.” All states have some form of sanctioning policy, which is to say that no
state relies only on positive work incentives to get people employed.
Time Limits. While all states are subject to the 60 month federal time limit for
individuals using TANF-related funds, they can also set shorter time limits, or can
provide state funding beyond 60 months.16 Seventeen states have time limits of less than
60 months for some families, 26 states use the 60 month federal time limit, and 8 states
have not imposed time limits which mandatorily end all benefits.17 For instance, several
of these states impose time limits on adult recipients but continue benefits for children
(Pavetti and Bloom, 2001).
Time limits should have two work-inducing effects. First, they should provide
incentives for recipients who might need welfare in the future to leave welfare as rapidly
as possible, in order to preserve future eligibility.18 This requires a thorough
understanding of the fact that “the clock is ticking” and some states have been better at
reminding recipients of this. There is some evidence that many recipients misunderstand


States are allowed to exempt up to 20 percent of their caseload from the 60-month time limit.
As in Tables 1 and 2, Washington, D.C.c is included as the 51st “state”.
For example, Swann (2000) develops a model indicating that time limits will have larger effects when
welfare recipients are forward looking.


where they are on their time clock (Bloom, 1999). Second, once time limits are imposed,
ex-recipients can no longer use cash assistance as a back-up to work.
Time limits have not yet been widely imposed; the first recipients did not begin
to hit the 60 month limit in most states until late 2001 or early 2002. As noted before,
there are somewhat perverse interactions between time limits and lower BRRs. In
addition, there is also evidence that time limits and sanctions interact in interesting ways.
Sanctions tend to affect the same less responsive and often more disadvantaged
population that is likely to hit time limits. This suggests that time limits may not have a
very large effect if many individuals will have already been removed from eligibility
through sanctions (Pavetti and Bloom, 2001).
Diversion. With no national entitlement to public assistance, states can deny
assistance to individuals. Many states have implemented eligibility determination
processes that encourage some applicants to be diverted from cash public assistance. Ten
states impose work search requirements on applicants prior to eligibility (i.e., applicants
must show that they’ve applied for a certain number of jobs as a condition of eligibility).
Twelve states provide short-term cash payments as an alternative to public assistance
eligibility, designed to meet some immediate need of the applicant which will then allow
her to return to work. Nine states use both techniques in order to divert applicants from
welfare, while 20 states make no effort at diversion.19
Work Support Subsidies. With more attention to moving welfare recipients into
work, states have also recognized the need to help families with work-related expenses.
States have greatly increased their expenditures on work support programs, primarily
child care subsidies. Between 1993 and 2000, federal funds available to the states for


child care subsidies rose from $9.5 billion to $18 billion, an 89 percent increase.20 States
are also helping to fund work transportation expenses, or job search expenses. Indeed,
more money is currently going into work support, including child care and transportation
subsidies, wage subsidies, as well as cash payments to working families, than into cash
assistance to non-working families (Gais, et. al., 2001).
While this review focuses primarily on the changes outlined above to cash
assistance and work-related programs, it is worth noting that these changes have had a
substantial impact on the utilization of other non-cash public assistance programs as well.
AFDC was historically the gateway program through which families were also certified
for Food Stamps or Medicaid. As access to cash assistance has fallen, Food Stamp usage
has fallen as well. 21 Working poor families seem to find it particularly difficult to access
Food Stamps. Offices are often open only during daytime hours and persons must
regularly report to the office in person to maintain eligibility. The complexity of
calculating Food Stamp amounts for working individuals, whose Food Stamp benefit
level will change from month to month as their earnings vary, often creates incentives for
caseworkers to try and get workers off the Food Stamp rolls. Arcane rules about the
resale value of a car and other assets limits can also restrict eligibility. The net result is a
program with very low participation among eligible families with a working adult head,
despite the declared goal of Food Stamps to provide assistance to all low-income
families. For instance, in 1999 only 43 percent of eligible persons with earnings were
receiving Food Stamps, while 70 percent of eligible nonearners were participating


For one of the few discussions of state diversion strategies, see Maloy, et. al. (1999).
Provided by Ron Haskins, based on calculations with data from the Congressional Research Service.
For further discussion of the problems with Food Stamp access post-PRWORA, see Greenstein and
Guyer (2001) and Zedlewski (2001).


(USDA, 2000). Of course, this may merely reflect an effort to structure the program so
that only the most needy among the eligible will actually participate, consistent with the
argument in Nichols and Zeckhauser (1982).22 Efforts are currently underway to reduce
these barriers to Food Stamp participation among working families.

III. Changes in Behavior and Well-Being Over the 1990s
At the same time as major changes in program structure occurred during the
1990s, there were also stunning changes in behavior. Strong adjectives are appropriate to
describe these behavioral changes. Nobody – of any political persuasion – predicted or
would have believed possible the magnitude of change that occurred in the behavior of
low-income single-parent families over this decade.
Caseload Changes. The most-discussed change over the 1990s was a remarkably
rapid decline in caseloads between 1994 and 2000, illustrated in Figure 3. The vertical
line indicates passage of the 1996 legislation. Between 1994 and 2000, caseloads
declined by 56.5 percent. Furthermore, these declines occurred everywhere in the nation,
with every state experiencing strong reductions in their welfare rolls.
Three things should be noted about the data underlying Figure 3. First, the rapid
caseload decline after 1994 was preceded by an unexpectedly strong increase in caseloads
in the early 1990s. Despite a relatively mild economic slowdown, caseloads rose 27
percent between 1990 and 1994. This rise in caseloads was one of the driving forces
behind the desire of state governors to implement more radical welfare reform. Ideally,
any theory that explains the caseload decline of the late 1990s should also explain the


As these numbers indicate, takeup rates among eligibles in means-tested programs are typically far below
one. For a discussion of takeup in the Food Stamp and the AFDC program, see Blank and Ruggles (1996).


caseload rise of the early 1990s. As discussed below, most researchers have focused on
the decline in caseloads without paying attention to the earlier rise.
Second, caseloads start to decline well before the enactment of the 1996
legislation, suggesting that legislation was not solely responsible for the caseload decline.
Third, the caseload decline in the late 1990s far exceeds anything in previous decades.
Despite relatively strong economic growth from 1983 to 1989, there is little evidence of
any change in caseload levels over that time period. This suggests that the economy
alone cannot explain caseload changes in the 1990s. The strong economic growth of the
1960s is actually correlated with a rise in caseloads. Most observers ascribe this to
increased take-up of welfare programs among the eligible following the launch of
President Lyndon Johnson’s War on Poverty (Moffitt, 1992). This at least suggests that
take-up changes might be important in the 1990s as well.
Labor Force Participation Changes. Changes in caseloads by themselves are not
very informative, and immediately lead to questions about the behavior and income of
those who are no longer receiving welfare. In particular, one of the major goals of the
1996 legislation and the policy changes that preceded it was to increase work effort
among welfare recipients. As it turns out, work effort soared over this time period among
single mothers with children.
Figure 4 presents labor force participation rates among women by marital status
and presence of children from 1989 through 2000. Unmarried women without children
work at a high and unchanged level throughout this time period. Married women, both
with and without children, show steady increases in labor force participation over the
1990s, at a slightly slower rate than in earlier decades.


In sharp contrast, single mothers with children show little change in their labor
force participation rates through the 1980s and into the mid-1990s. But between 1994
and 1999 their labor force participation rises by 10 percentage points. Among single
mothers with children under the age of six, labor force participation rates rise by 5
percentage points. In short, at exactly the same time as caseloads start to fall, work effort
rises substantially among exactly the population most affected by the caseload declines.
This provides at least prima facae evidence that the caseload declines were associated
with increases in work. Other available data supports the idea that women are moving
from welfare to work at a high rate. Among those who report receiving public assistance
income in the previous year, the share reporting themselves employed in March of the
following year rises from 19.8 percent in 1990 to 44.3 percent in 2000.23
Even among women who remain on welfare, work effort rises strongly. This may
reflect both the greater effort to move welfare recipients into work, as well as the lower
benefit reduction rates that continue subsidies to working women as their earnings rise.
Among women on welfare, the share with earnings rises from 6.7 percent in 1990 to 28.1
percent by 1999.24
Increases in work not only increase earnings and add to immediate family income,
but may also build labor force experience that leads to higher wages over time. Gladden
and Taber (2000) indicate that even among low-skilled women wages increase with


Calculated by the author from March Current Population Survey data. Bishop (1998) also provides
detailed information on labor supply increases among never-married women in the 1990s.
This is all the more remarkable in light of the amazing inelasticity of work effort among welfare
recipients in previous decades, discussed by Moffitt (1992). The 1990 data is from U.S. House of
Representatives (1998, Table 7-19); The 1999 data is from U.S. DHHS (2000, Table 3:3.c).


Changes in Income and Poverty. Declines in public assistance usage and
increases in labor market involvement may or may not signal income increases, since
reductions in welfare benefits will offset increases in earnings. Hence, there has been a
great deal of interest in whether incomes have risen among less-skilled single mothers.
The official U.S. poverty data suggest unambiguous improvements in poverty
among single-mother families, as Table 3 indicates. The share of all families in poverty
declines from 11.9 in 1992 (the end of the recession in the early 1990s) to 8.6 percent in
2000, below the previous historic low of 8.8 percent in 1974.25 Given the strong
economy, this is perhaps a disappointingly small decline in poverty. Poverty among
single-mother families declines more rapidly however, from 35.4 percent in 1992 to 24.7
percent in 2000, a new historic low. Poverty rates among single mother families headed
by blacks and Hispanics were also at historic lows in 2000. This suggests that, at least in
the short run, changes in social policy did not worsen the economic situation of poor
households. The decline in poverty is far less, however, than the reduction in public
assistance caseloads. As a result, the share of working poor in the U.S. population rose,
as some women left public assistance for employment but remained poor.
Unfortunately, U.S. poverty rates provide only partial information on well-being
(Citro and Michael, 1995).26 Table 4 provides information on poverty gaps among
families with children between 1993 and 1999, showing how far average family income
is below the poverty line among poor families. Row one shows the poverty gap based
only on pre-transfer income among families. Row two includes social insurance benefits


All official poverty rate data can be found at www.census.gov.
Alternative poverty calculations can be found in U.S. Department of Commerce (1999), with updated
numbers for 1998 at www.census.gov/poverty/povmeas/expov.tabe.html. These calculations also show a
strong decline in poverty among female-headed families over the 1990s.


(Social Security, disability and workers compensation), row three adds means-tested
benefits (cash and in-kind), and row four calculates poverty gaps based on total income
net of taxes. The bottom part of the table shows the percentage reduction in the poverty
gap as the definition of income is sequentially expanded.
Between 1993 and 1999 substantial increases in earnings resulted in a declining
poverty gap when looking only at pre-transfer cash income. With increases in earnings
come reductions in means-tested benefits, however. Social Insurance reduces the poverty
gap by a relatively constant 16 to 18 percent over these years. Means-tested benefits,
however, reduce the poverty gap 44 percent in 1993, but only 34 percent in 1999,
reflecting the declining caseloads. Over time, the federal tax system expands to further
reduce poverty gaps, largely because of the growth in the EITC. The net result is a slight
rise in poverty gaps based on after-tax income over the 1990s, from $1447 to $1524. Of
course, since fewer persons are in poverty by the end of this period, it is hard to state
whether the net effect is to raise or lower well-being. A more disadvantaged group may
remain poor over this period, resulting in a rising poverty gap.
Table 5 presents information on a set of tabulations recently completed by the
Center on Budget and Policy Priorities,27 which calculate the average income of femaleheaded households by quintile. The results in Table 5 indicate that incomes among
women in the top 80 percent of the income distribution of female-headed families
(quintiles 2 through 5) rose unambiguously over the 1990s, including increases post1996. This is consistent with evidence from other surveys that do similar data tabulations
(Primus, et. al., 1999; Haskins, 2001; Gabe, 2001, Jencks, Swingle, and Winship, 2001).


These data are currently unpublished, but available upon request from Wendell Primus.


There is other evidence that some group of disadvantaged women lost income in
the mid-1990s. Haskins (2001) discusses evidence of a rise in deep poverty (the number
of persons at less than 50 percent of the poverty line) in the mid-1990s. The very poorest
quintile of single-mother families experienced an increase in income in the first half of
the 1990s, but little overall income growth post-1996. This is not surprising, as
underlying calculations indicate that means-tested income among this population fell by
more than $1500, while earnings rose by less than $1000. In higher quintiles, earnings
gains were much stronger than the loss in means-tested income. Zedlewski, et. al. (2002)
also document rises in deep poverty between 1996 and 1998 among families with
Somewhat contrasting evidence comes from data on consumer expenditures,
which shows increases in consumption spending through the 1990s, even among very
low-income single mothers with children (Haskins, 2001; Meyer and Sullivan, 2001).
Jencks, et. al., (2001) indicate that food-related problems declined between 1995 and
1999 for single mothers as rapidly as among other poor groups. In short, the available
evidence suggests that most single mothers gained ground in the 1990s, but there is a
group of the poorest single mother families who have made only minimal gains over the
1990s and some at the very bottom who might have lost ground.
All of these income calculations should be viewed with some skepticism. First, a
substantial minority of those leaving welfare appear to be unemployed at some later point
(Brauner and Loprest, 1999). We have little evidence on how these women are
surviving, but the best guess is that they are relying more upon boyfriends or other family
members for income. While this may be a viable short-term strategy, over time such


arrangements may fall apart and are unlikely to provide long-term economic stability for
either the women or their children.
Second, few of these studies actually measure disposable income. While the
studies cited above take into account the EITC and some other non-cash transfers, they
do not fully calculate tax rates on earners. They typically impute EITC receipt and their
data on housing, Food Stamps or medical assistance is not complete. They provide little
information on income sharing with other individuals or families. Furthermore, none of
these calculations take account of increased expenses associated with work, particularly
out-of-pocket child care expenses. There is a need for research that provides a more
complete picture of the changes in the actual economic well-being of less-skilled singlemother families and their children over the 1990s, in the midst of major policy and
behavioral changes.

IV. Research and Evaluation Challenges
Estimating the effects of the program changes described above creates real
evaluation challenges. One must control effectively enough for all other environmental
influences to produce a credible estimate of a policy effect. This is particularly difficult
in a world where many things are changing at the same time, as happened in the 1990s.
Past work evaluating the AFDC program tended to describe the welfare
environment for an individual by controlling for state benefit levels and (occasionally) for
effective state BRRs. Since most eligibility rules were uniformly set by the federal
government, state variation in benefit levels was the dominant feature describing welfare
generosity and access across states.


Post-1996, it is much more difficult to characterize the policy environment for
each state. State welfare policies vary along multiple program dimensions, and the
precise nature of the bundle matters since different program components may interact
with each other. For instance, one may need to control for the interaction of BRRs and
sanctions, rather than just controlling for each separately. Not all of the program
elements described above are easily coded, and there is little guidance in the research to
date showing the most effective way to measure and code some of the newer policies like
time limits, sanctions or diversion activities. In some cases only a few states have
adopted particular policies or combinations of policies. For data sets with state level
observations, this can make it difficult to estimate precise policy effects.
With individual-level data, it is much more difficult to identify the specific
program rules facing any individual. Data sets like the Current Population Survey
provide no information on whether an individual is required to participate in a welfare-towork program, whether they have been sanctioned, how close they are to reaching their
time limits, what type of subsidies for child care or other work supports they might be
receiving from TANF dollars, or whether they receive EITC funds. In short, most of our
data sets are designed to collect information on cash welfare assistance, appropriate for
the old world of AFDC but not very useful in the new world of TANF where cash public
assistance levels are less and less descriptive of state welfare programs.
For all of these reasons, it has become much harder to study the impact of welfare
programs or their specific components on individual behavior. The complexity and
diversity in state programs means that an increasing amount of analysis focuses on data
from a single state, creating problems of comparability and generalizability. Closely


linked to this focus on single states, there has been a substantial increase in the use of
administrative data to analyze welfare-related questions. Administrative data typically
provide more detailed information on the parameters of the welfare system that impact
any individual, including their use of multiple programs, their work requirements, their
accumulated timing of welfare receipt, and so on. More and more researchers are
linking information from multiple administrative data sets. For instance, welfare receipt
records might be linked with unemployment insurance records to determine quarterly
earnings after leaving welfare.
Most researchers have tried to measure the direct effects of the enactment of
waivers and the implementation of TANF. This is complicated not only by the data
problems mentioned above, but also by other evaluation difficulties.
First, waivers were not implemented by a random set of states. States with higher
unemployment rates were more likely to request major welfare waivers (Schoeni and
Blank, 2000). This means that waivers cannot be used as a simple “natural experiment”
in which results in waiver states are compared with results in non-waiver states.
Second, the coincidence and the interaction of the economic expansion and the
implementation of welfare reform creates problems. The strong economic boom and the
passage of PRWORA occur simultaneously and it is difficult to separately identify their
causal effects. This is even more true if the two events interact with each other. For
instance, states may have been able to change their cash public assistance programs to
work-oriented support programs more quickly and more thoroughly because they did not
have to worry about job availability issues. Most people who could be placed in a job
search assistance program were able to locate a job. Conversely, the strong push that


increased the supply of less skilled women into the labor market may have changed the
demand side of the labor market in some places, for these women and for other less
skilled workers (Bartik, 2000). For all of these reasons, separating economic effects
from policy effects promises to be difficult in the mid-1990s.
Third, multiple policy changes were being implemented at the same time, and
these policy changes almost surely interacted with each other in a reinforcing way. The
large increases in the EITC subsidies occurred just before welfare reform was passed and
at the same time as minimum wage increases in the mid-1990s. As noted above, child
support subsidies were restructured at the same time as welfare was reformed. This
makes it difficult to separately identify individual policy effects. For instance, Blank
(2000) argues that it was the combined interaction between multiple policy changes and a
booming economy that led to the unexpectedly large caseload declines and labor force
participation increases.
Fourth, the implementation of state TANF programs is particularly difficult to
evaluate because it occurred at about the same time in all states. Within a nine-month
period from September 1996 through July 1997, all states began implementing their new
TANF plans. This is in contrast to major state waivers, which were approved over a four
year period in 27 states, allowing a researcher to identify the effects of these waivers
from the differences in when they were implemented across states.
Finally, almost ignored in the economics literature, there is often a difference
between enacted program rules and actual implementation practices. This may be
particularly true for a major program change that is being implemented quickly. Because
staff are not fully trained in the new systems or because staff may disagree with some of


the new program changes, what’s actually done “on the ground” could differ substantially
from the formal description of state programs (Meyers, Glaser, and MacDonald, 1998;
Gais, et. al., 2001).
A multiplicity of empirical approaches have been used to study the welfare policy
changes of the 1990s. Three of the most common are summarized here, with a brief
discussion of their pros and cons.28
Random Assignment Experiments. For more than two decades, researchers have
studied labor market interventions with random assignment experiments. In these cases,
an experimental group is randomly chosen from among those eligible for a program and
this group receives the services and program benefits. An alternative control group is
refused entrance into the program and operates in an environment (presumably)
unaffected by the program. If randomization is done correctly, the only difference
between the two groups should be that one group receives the program treatment and one
does not. That means that simple outcome differences between the groups can be used as
a measure of program effects.
Experimental evaluation of welfare-to-work programs has occurred since the mid1980s and became quite sophisticated by the 1990s. During the 1980s these experimental
evaluations focused solely on welfare-to-work programs. The use of waivers in the
1990s allowed states to implement more extensive reforms involving other program
changes beyond welfare-to-work efforts. Because the Department of Health and Human
Services required experimental evaluations of waiver programs, a body of results are now
available from pre-1996 state programs analyzing the impact of more complex welfare


In addition to these three approaches, there is a great deal of more descriptive work, much of it involving
the collection of new data, including a variety of ethnographic studies in particular neighborhoods.


reforms with multiple components – welfare-to-work training, time limits, sanctions,
family caps, etc -- on AFDC receipt and earnings.29 The federal mandate for
experimental evaluations of waiver programs ended when TANF was implemented and
there have been no experimental evaluations of TANF programs post-1996.
These experimental evaluations are viewed as highly credible, since they come as
close to a controlled research environment as possible. When experiments are
appropriately designed, there is no better methodology available. Indeed, the widespread
acceptance of the positive results of welfare-to-work evaluations in the 1980s were a
major reason why policymakers supported work-oriented welfare reform in the 1990s.
These experiments have limitations as a way to study the welfare reforms of the
1990s, however. First, when multiple program changes are occurring, it is difficult to
study the separate effects of individual program changes in an experimental way. Hence,
the policy implications of experimental results were more interpretable in narrowly
implemented welfare-to-work programs (which changed only one or two program
parameters) than in broad waiver programs (which typically involved multiple program
changes). For instance, it is not possible to separately identify the effect of time limits
from other welfare-to-work components in existing experimental evaluations from the
early 1990s; the experimental results identify the aggregate effect of all program changes
together rather than the specific effect of each individual program change. Similarly, it is
not possible to use experimental evaluations to study the impact of a legislative change
(such as TANF) where multiple changes are implemented throughout the state at the
same time.


See Gueron and Pauly (1991) and Friedlander and Burtless (1995) for a summary of much of the earlier
research, and Bloom and Michalopoulos (2001) for a summary of some of the key 1990s research.


Second, experiments should be designed so that the program effects cannot
influence the control group. With all of the simultaneous policy changes occurring in the
1990s, however, it was hard to prevent some contamination. Word circulated among
welfare recipients – including the control group – about mandatory work requirements or
upcoming time limits. This might lead the control group to respond to these rumors, even
though they were formally unaffected by the changes.
Third, experimental studies are expensive and time-intensive. They almost
always require collecting additional survey data, both at baseline (when the control and
experimental groups are defined) and at multiple follow-up study points. Because their
implementation takes skill and often requires some administrative reorganization within
welfare programs to separate the control and experimental groups, they put additional
demands on administrators and front-line workers. In the midst of all the other changes
occurring in welfare offices, few states wanted to invest either the funds or the time
necessary for experimental evaluations over the late 1990s.30 The locations that did
participate in earlier experimental evaluations during the 1990s are not a random sample
of all states or welfare offices. For instance, we have a number of excellent evaluations
done in north midwestern states and fewer evaluations done in the traditional “deep
south” states. This can call into question the generalizability of the experimental
Fourth, these experimental studies are not well-designed to study “entry effects.”
An experimental program may not induce the same discouraging effect on welfare usage


A variety of waiver evaluations were ongoing and continued into the post-1996 period. Post-TANF,
many governors pointed to the declines in caseloads and the implementation of welfare reform as a major
success. This could have made them more reluctant to authorize serious evaluations that might reduce their
ability to garner political credit from these changes.


that might result from a permanent welfare reform, hence caseload change may be
underestimated. Even if some families are discouraged by the experiment from ever
applying for welfare at all, this effect is typically not measured in most experiments.31
For all of these reasons, the experimental evidence on the effects of welfare
reform is highly useful where it looks at the impact of specific program components in
particular types of welfare programs. But the experimental evidence tells us relatively
little about the overall effects of TANF implementation in states in the mid-1990s.
Leavers’ Studies. A substantial amount of research time and money has been
devoted to following persons as they left welfare in recent years. A number of
organizations and individuals launched so-called “leavers’ studies” soon after the
implementation of the 1996 legislation. The primary intent was to analyze the behavior
and well-being of those who lose welfare benefits (either voluntarily or involuntarily) in
the post-reform era.
Leavers’ studies answer a very specific policy question, namely, “How are people
faring who used to receive public assistance but are no longer on the rolls?” The interest
in this question has been strong, particularly as caseloads have declined so precipitously
in most states.
Most of these studies use a combination of administrative data and new survey
data. Persons on welfare at a specific point in time are tracked and surveyed at some later
point, to ask about their employment, family, and income situation. This survey
information may be combined with other administrative data to investigate program
receipt of Food Stamps, Medicaid, or other support programs, to measure recidivism

An alternative version of entry effects occurs if a program induces additional welfare participation. This
seems less relevant to the welfare reforms of the 1990s, which tended to focus on moving people directly


(return to cash public assistance), or to verify employment using Unemployment
Insurance program data on earnings and employment. These studies can provide quite
detailed information on the behavior of ex-welfare recipients.
Like experimental evaluations, leavers’ studies can be complex, costly, and timeconsuming. It is often difficult to locate and survey ex-welfare recipients, and a number
of not-very-credible leavers’ studies have low (and presumably quite selective) response
rates. Working with administrative records, particularly records across multiple
programs, requires matching individual identifiers and dealing with complex data
problems. As a result, the quality of leavers’ studies varies greatly. Since most leavers’
studies are state-specific, it is often difficult to compare them as different researchers
focus on different outcomes or use different methodologies in different states.
The biggest limitation to leavers’ studies is that they provide very little
information about policy effects. Unlike an experimental evaluation, it is impossible to
separate those who would have left welfare even under AFDC from those additional
leavers due to the new welfare program design. This means leavers’ studies tell us
almost nothing about the effects of new programs.32
Furthermore, leavers’ studies by design focus on a limited population--those who
were once on welfare. Some studies ignore those who remain on welfare longer, a group
of some concern. None of these leavers’ studies say anything about those who might
have come onto AFDC pre-1996 but who chose not to come onto TANF post-1996.
Evidence suggests that both entry into welfare has fallen and exits from welfare have

into jobs; in contrast, the reforms of the 1980s often had substantial education and training components.
An exception is Cancian, et. al. (2002), who compare pre-reform leavers with post-reform leavers in the
state of Wisconsin. While this is a superior methodology, even these estimates are contaminated by other
changes (such as the booming economy) which occur at the same time as reform.


risen (Mueser, et. al., 2000). To the extent that those who are diverted from receiving
welfare are differently selected from those who come on but leave faster, the leavers’
studies cannot be interpreted as evidence on the general well-being of persons affected by
welfare reform. One might expect leavers to be somewhat less employable and more
disadvantaged than those who have options that allow them to choose not to enter welfare
in the first place.
In short, leavers’ studies provide little information about the overall effects of
welfare reform. At best they tell us something descriptive about how a specific
population of ex-welfare recipients is faring, but it is difficult to interpret anything causal
about policy (or any other explanatory variable) from these studies.
Econometric evaluations. A growing body of literature uses a combination of
national and administrative data to study the impact of policies. Typically, these studies
use data on a key dependent variable – such as caseloads or labor force participation -from multiple years and regress it against controls for economic factors and policy
factors. Some studies also include controls for demographics and political changes.
Much of this work is based on state panel data. For instance, state caseload data might be
regressed against state unemployment rates, state AFDC/TANF benefit levels, and
dummy variables that signal the implementation of a state waiver. Alternatively, some of
this research utilizes individual data on welfare participation or work behavior for
multiple years.
A typical regression equation based on state panel data is as follows:

Yst = α s + β t + δPst + γX st + ε st .


where Yst is the dependent variable (say AFDC/TANF caseloads) in state s in year t. The
vector αs represents the set of estimated state fixed effects for all s states, βt represents a
set of year fixed effects for all t years (sometimes there are also state-specific time trends
included), Pst is a set of policy-specific parameters and δ is its related coefficient vector,
while Xst is a set of all other included variables with γ its related coefficient vector. Xst
typically includes state unemployment rates and may include other state economic and
demographic variables. Equation (1) is usually estimated with a weighted least squares
estimation procedure, with weights based on state population.33
Policy variables are typically represented as dummy variables that equal zero
prior to the implementation of a specific policy (a waiver or a TANF program), and equal
1 in each year thereafter.34 Hence, the policy coefficients measure the average change in
Y after the policy change, controlling for all other variables. The state effects remove
long-term state-specific differences and allow one to interpret the coefficients as the
effect of changes in the independent variables over time within a given state. The year
effects remove any common changes occurring in all states in the same year (and hence
remove the effects of policies that are implemented everywhere at once, such as an EITC
change or a minimum wage change).
Identifying the true effects of policy on the dependent variable Y requires several
things: First, policies must be accurately and completely coded; second, there must be a
way to identify the policy effects separately from the other variables; and third, there
must be no omitted variables correlated with the policy changes to bias the policy

Even if individual level data is available some researchers aggregate this to the state level, arguing that
the variables of interest (policy differences within and across states) vary only at the state level. In a few
cases, authors interact policies with individual-level characteristics, in which case utilizing individual-level
data is a necessity.


coefficients. Most researchers use relatively sparse specifications, hoping that state and
year fixed effects and state-year time trends will control for the large number of omitted
variables that inevitably haunt these econometric exercises.
As discussed below, most of this work has focused on AFDC/TANF receipt,
looking at caseload changes over time as the dependent variable. Some papers look also
at changes in labor force participation over time, and a few papers use earnings, income,
poverty, fertility or marriage rates as the dependent variable.
These econometric studies confront a variety of problems. First, identifying the
policy effects can be a problem. The effects of welfare waivers are reasonably well
identified, since different states adopted these waivers at different points in time. The
effects of TANF implementation are much less well-identified. As noted above, virtually
all states implement TANF at about the same point in time. Most papers try to use the
differences in timing over 1996-97 to identify an effect, but the standard errors of these
estimates are high.35 Some papers try to identify effects by combining waivers and
TANF, coding a dummy variable that equals one if a state has a major waiver in effect or
if it has adopted a TANF program. This has the odd effect of forcing waivers and TANF
programs to have identical effects, almost surely not justified given how much more
extensive were the changes involved with state TANF plans.
Even if identification were easier, this research merely estimates the aggregate
effect of these changes, without differentiating between the very different set of waiver or
TANF program components adopted by different states. Hence, some researchers have

In the year the policy is enacted, the dummy variable is typically equal to the fraction of months that the
policy is in effect.


tried to code the adoption of specific program components rather than the adoption of a
single policy change.36 Unfortunately, the identification problems with this approach are
severe. As noted above, it is not clear how to code some policy changes (and we have
only limited information post-1996 on what specific states are doing in certain policy
areas). Furthermore, some individual policies are adopted by so few states (and only in
the few years post-1996) that there is not enough information to estimate a reliable
coefficient. The result is that much of the econometric literature focusing on individual
policy components finds insignificant or even perverse coefficients.
Finally, there have been substantial specification arguments in this literature.
Most papers have chosen to utilize a simple panel data framework with fixed effects,
perhaps including lags on a few key variables (like unemployment rates). A few papers,
however, have chosen more complex specifications, including lagged dependent
variables, a greater number of lags on key independent variables, and/or more extensive
fixed effects. These choices matter because the more complex specifications typically
find smaller or less significant policy effects. Those who like these latter papers tend to
argue that the more complex specifications better mirror reality and are more reliable.
Those who find these latter papers less persuasive (including myself) tend to argue that
they are overspecified, with extensive lag structures that leave little scope for measuring


See the discussion of identification problems in Schoeni and Blank (2000). They try an alternative way
to estimate TANF effects based on a difference-in-difference estimates, pre- and post-1996 and between
more and less educated women.
Rather than controlling for the implementation of waivers, for instance, this could mean controlling for
the type of sanctions approved in the waiver, the presence and length of time limits, the implementation of
a family cap, or the nature of the work mandates in the state.


policy effects based on simple dummy variables. In addition, the combination of a
lagged dependent variable with state fixed effects produces inconsistent estimates.37
A seminal contribution to this specification argument was provided by Klerman
and Haider (2001), who point out that there is no clear theoretical justification provided
for any of the specifications used in earlier papers. They note that the stock of welfare
cases is the result of flows into and out of welfare. They model the dynamic process of
entering and leaving welfare and derive an estimable model of aggregate caseload change
from this. They show that even if the entry rate and the continuation rate are functions
only of contemporaneous economic conditions, per capita caseloads will be a non-linear
function of lagged economic conditions equal to the longest period individuals are on aid.
Hence, only particular lagged specifications are correct. They also indicate the
conditions under which including a lagged dependent variable is appropriate.
Klerman and Haider’s work provides a more believable and persuasive
specification than earlier papers, and suggests that much of the other research estimating
the determinants of per capita caseload levels has been misspecified. Klerman and
Haider prefer a model which estimates welfare entry and exit flows, rather than net
caseload levels. Unfortunately, estimating this specification requires flow data, which
does not appear to be reliably available at the national level. (Klerman and Haider
estimate their model on California data only, where they believe they have reliable data.
This makes it hard to generalize their results and compare them to other work.) Klerman
and Haider’s results from this co-called “stock-flow model” are closer to those of the
simpler specifications in the role that it ascribes to the economy over the 1990s.

See the discussion of these specification issues in Grogger, Karoly and Klerman (2002) or Blank
(2001b). For a more positive reading of these results, see Bell (2001) or Ziliak (2002). Moffitt


Ultimately, econometric models – however limited – will probably provide the
best evidence we are likely to have available on the overall effects of welfare reform.
Such models are almost surely less reliable in providing evidence on individual program
components; when available, experimental evidence on specific program changes is
probably more believable. Future research should focus on better ways of utilizing
econometrics to identify individual welfare program components.
For instance, Grogger (2000, 2002, forthcoming) takes a clever approach with
time limits. He notes that families with young children should be more affected by time
limits than families with older children (since families with young children have a longer
period of future potential welfare eligibility). Hence, he interacts state time limit
information with information on the ages of children in a household, and finds
substantially larger effects among families with younger children, as hypothesized.
Similar creativity in teasing out the effects of other specific program components would
be useful.
The remainder of this paper summarizes the research findings from papers that
use the above methodological approaches. I organize this review by the dependent
variable in the paper.



The most voluminous literature on welfare reform in the past decade has focused
on caseload changes. Interestingly, prior to the mid-1990s, there was virtually no
published literature in economics journals looking at movements in caseloads over time,38

(forthcoming) also provides a summary of this literature.
An exception is Moffitt (1987).



but the number of more recent articles is growing rapidly. The primary interest in this
research literature is to explore the steep caseload decline that started in the mid-1990s,
with particular attention to separating out the effects of economy from policy.
Almost all of the literature on caseloads fits into the third methodology described
above, and utilizes regression analysis on some sort of panel data over time. (Some
evidence from experimental studies on the impact of specific program choices on welfare
usage is discussed in Section VIII below.) Different papers focus on different variables,
and the discussion below focuses sequentially on the effects of economic variables and of
aggregate policy variables on caseloads. I briefly discuss the (few) papers which focus
on caseload flows rather than caseload levels, followed by a discussion of research that
distinquishes the effects of specific policy components on caseloads. I close this section
with a short discussion of the literature on food stamp caseloads.
Table 6 provides a list of the papers to date that use regression analysis to
investigate the effects of welfare reform during the 1990s, indicating the dependent
variable, data source, primary included variables, and a few key conclusions. In most of
these papers, caseloads are the dependent variable, although a few of them (discussed
below) look at employment, income, and family structure changes as well. Part A of
Table 6 lists the papers using data prior to the implementation of TANF, which primarily
focus on the effects of state waivers. As we discuss below, some of these papers focus on
the implementation of any waiver, while others try to differentiate between the policy
components in different waivers. Part B lists the papers that utilize data post-TANF and


that estimate the effects of TANF as well as waivers. Part C lists the papers that use flow
data on exits from or entries onto welfare, rather than stock data on caseloads.39
Aggregate Caseloads and the Economy. The majority of papers utilize annual
state panel data, based on administrative records, to study movements in total
AFDC/TANF caseloads, using some variant of equation (1). The typical economic
variable is the state unemployment rate, although a few papers use state income or wage
information as well. This is due to data convenience as much as anything else -- state
unemployment rates are one of the few readily available annual state-level economic
variables. Given the sensitivity of less-skilled workers to movements in unemployment
(Hoynes, 2000), this is often assumed to be reasonable characterization of the economic
The majority of papers find relatively similar effects of unemployment on
caseloads, not surprising since these papers tend to use similar methodologies and data
sets. For instance, Council of Economic Advisers (1997, 1999), Levine and Whitmore
(1998), Wallace and Blank (1999), and Blank (2001a) all find that a 1-point rise in
unemployment tends to increase caseloads by about 5 to 7 percent. Blank (2001a)
suggests that these effects are larger for the small part of the caseload composed of
married couples than among single mothers.
Most of these papers attempt to see how much of the caseload change over the
mid-1990s can be ascribed to economic changes. For instance, Council of Economic
Advisers (1999) indicates that changes in unemployment explain 26 to 35 percent of the

I do not include papers based on data from one state only in Table 6. A number of good state-specific
research exists, such as MaCurdy, Mancuso, and O’Brien-Strain (2002) for California. I also omit studies
that are based on a single cross-section rather than panel data (such as Mead, 2000.)


caseload change in 1993-96, but only 8 to 10 percent of the caseload change in 1996-98.
These estimates range widely across studies, and are highly affected by the years over
which they are estimated and by the specification. Specifications utilizing lagged
dependent variables and/or first differences (Ziliak, et. al., 2000; Figlio and Ziliak, 1999)
tend to find larger effects due to economic changes.41
It also appears that the responsiveness of caseloads to unemployment has
increased over time (Moffitt, 1999a; Council of Economic Advisers, 1999). This means
that studies based on more recent and shorter panels (such as Ziliak, et. al., 2000) are
more likely to find larger unemployment effects. While the reasons for this change are
unclear, it is consistent with a welfare system that is doing more and more to emphasize
work. This reduces the dependence of welfare recipients on cash benefits, and increases
their dependence upon job availability.42
Several of the papers that utilize data post-1996 and compare the TANF era with
the AFDC era indicate that unemployment effects on caseloads are smaller post-1996
than pre-1996 (Council of Economic Advisers, 1999; Wallace and Blank, 1999; Schoeni
and Blank, 2000; O’Neill and Hill, 2001). Post-1996, public assistance programs had a
harder edge and put more attention into enforcing time limits, sanctions, and diversion
policies. Given this policy environment, it may not be surprising that the economy
mattered less to caseload changes during this time. Alternatively, the very strong
economy of the late 1990s might have been expected to have a greater effect than the
more sluggish economy of the early 1990s, in which case this is a surprising finding.

This assumption is typically made without real evidence. As discussed below, other economic variables
also appear to be important over the past two decades in explaining caseloads.
Klerman and Haider (2001) indicate that these specifications should bias the economic effects upward.


A few studies have gone beyond attention to state unemployment rates and
utilized a richer set of economic variables. Several studies include information on statespecific minimum wages (Council of Economic Advisers, 1999; Grogger, 2000), on
employment/population ratios (Ziliak, et. al, 2000) or on state income levels (Schoeni and
Blank, 2000). Several studies have tried to characterize the shifts in relative wages and in
industry mix that occur over the 1980s and 1990s. Blank (2001a) calculates state-specific
average wage levels as well as 50th percentile/10th percentile wage level ratios within
each state and year. Bartik and Eberts (1999) utilize data on the education requirements,
wage premiums, and low-wage employment implied by the industry mix in each state and
year. In most cases, these additional variables are significant and suggest that more than
the unemployment rate matters in affecting caseloads. Blank (2001a), however, indicates
that the estimated unemployment effect is relatively unchanged by the inclusion of
demographic or political variables.
Virtually all research agrees that state economies had a significant effect on
caseloads, and that caseloads rise in bad economic times and decline in good times. Most
of the research suggests, however, that economic changes alone cannot explain the
majority of caseload movements over the 1990s; policy variables also matter.
Aggregate Caseloads and Overall Policy Effects. Policy shifts are typically
characterized by dummy variables that “turn on” when a policy is implemented in the
state. Early papers focused particularly on the effects of state waivers. More recent
papers have also tried to investigate the impact of TANF implementation. The


Bartik and Eberts (1999) suggest this might be due to declining demand for less skilled labor, which
could make joblessness increasingly difficult to escape for low-wage workers.


identification problems discussed in the previous section make the latter particularly
difficult to estimate.
Most of the literature finds that state waivers implemented in the first half of the
1990s had a significant and negative effect on caseloads.43 For instance, one of the
earliest studies finds that the implementation of major statewide waivers explains about
13 to 31 percent of state caseload change between 1993 and 1996 (Council of Economic
Advisers, 1997). While the magnitude of impact varies somewhat across studies, similar
results are found in Levine and Whitmore (1998), Wallace and Blank (1999), and Blank
(2001a). Moffitt (1999a) and Schoeni and Blank (2000) use somewhat different data than
other studies, aggregating individual data into state-year observations on AFDC
participation by women’s age and education level. Both of these papers also find
significant negative waiver effects on AFDC participation, with particularly strong
effects among less educated women, consistent with the expected impact of welfare
Fewer studies have looked at the impact of TANF implementation (Part B of
Table 6). Council of Economic Advisers (1999) and Schoeni and Blank (2000) both
indicate that TANF appears to have a larger effect on caseloads than did waivers.44 This
is consistent with the evidence cited above that shows that economic factors had smaller
effects post-TANF, suggesting that the policy changes of the mid-1990s were a major
cause of declining caseloads.


As discussed above, these waivers were not randomly implemented across states. Once one controls for
differences in state unemployment rates, non-waiver states and waiver states show similar caseload trends
prior to the implementation of waivers (Schoeni and Blank, 2000)
Wallace and Blank (1999) and Grogger (2000) find TANF effects that are similar in magnitude to
waivers, but both papers only have data through 1998. This is before the full effects of state TANF
programs might have been felt.


A few studies find almost no effects of policy, although most of these are
focusing on the waiver period and not the post-TANF period (Ziliak, et. al., 2000; Figlio
and Ziliak, 1999). These studies, as discussed above, tend to use more complex
specifications. The shorter time period in Ziliak, et. al. (2000) also makes it more
difficult to separately identify policy and economy effects. Other specification issues
matter as well, including the choice of fixed effects. For instance, Schiller (1999)
includes no fixed effects and (not surprisingly) finds stronger state policy-related effects.
O’Neill and Hill (2001) do not include year fixed effects and as a result their estimated
coefficient on the TANF dummy variable over the late 1990s is much larger than in other
Despite evaluation and methodological problems, the bulk of the research
literature suggests that the policy changes over the 1990s were important to the rapid
caseload decline. This evidence remains unsatisfying, however, for a variety of reasons.
First, most of these papers focus on aggregate policy changes (the adoption of a major
state waiver or the implementation of a TANF plan) rather than on specific policy
components. For instance, some aspects of these waivers (time limits and stricter
sanctions) might have been expected to reduce caseloads. Other aspects (lower benefit
reduction rates) might have increased caseloads. I discuss the efforts to characterize and
measure the impact of policy specifics below.
Second, it remains very difficult in any of this literature to separate economic and
policy effects, given the extent to which these were interacting with each other over the
late 1990s. The combination of extremely strong economic growth with rapid policy
change means that both effects were reinforcing each other.


Third, while these papers focus on welfare-related policies, they are less useful in
measuring the additional impacts of other policy changes over this time period. Because
of the nature of the models (typically including year fixed effects) the impact of changes
in the EITC or minimum wage on caseloads are difficult to evaluate. No one has yet put
together the appropriate data to measure the impacts of changes in child support policy,
child care subsidies, or health insurance. To the extent that these other changes are
interacting with the measured policies over time, estimates of the measured policies may
be biased up or down.
While there remains a very strong interest in the question “what has been the
effect of the policy changes of the 1990s on caseloads (and other variables as well)?” it
remains a difficult question to answer in an entirely credible manner. Future research in
this area, with better data or better identification strategies, will be received with interest.
Caseload Entry and Exits. Aggregate caseload changes are the result of an
underlying dynamic process in which individuals are choosing to enter welfare and
choosing how long to stay on it. In other areas, looking at these underlying dynamic
processes has produced new insights about net changes.45 A few papers, listed in Table
6, part C, have tried to investigate the underlying flows in and out of public assistance.
This is hard to do because there does not exist good national flow data on
AFDC/TANF entry and exit. While states have reported welfare entries and exits for
many years, this data has severe problems. It is inconsistently reported across states
(states define entries and exits differently) and some entries and exits appear not to be
reported. For instance, if one aggregates entries and exits over the 1980s and 1990s in


For instance, the literature on employment and unemployment has benefited by looking at flows in and
out of the labor market and in and out of employment.


many states, there is little evidence of the significant rise in caseloads that is visible in the
aggregate caseload data, suggesting either that entries are consistently undercounted or
exits are overcounted.46
Klerman and Haider (2001) provide a model of dynamic flows in and out of
welfare, and relate them to the net caseload. As discussed above, they also critique
previous econometric estimates as misspecified, based on their model. They utilize
county-level entry and exit data from the state of California only, which they believe to
be accurate, to estimate the determinants of entry and exit. Their results on the role of
unemployment in caseload changes based on flow models are quite similar to those
estimated in much of the literature using stock models, and indicate that the economy
accounts for less than half of the caseload change in the mid-1990s.
Mueser, et. al. (2000) take a somewhat similar approach. They use administrative
data on welfare recipients from five major metropolitan areas to create their own entry
and exit rate calculations. Using data over a number of years in the mid-1990s, they
estimate that about two-thirds of the decline in welfare is due to higher exits from
welfare, while about one-third is due to lower entry. Consistent with the literature on
aggregate caseloads, both state economic conditions and policy changes affect welfare
exits. Welfare entry appears less affected by the economy.
Finally, Hofferth, Stanhope and Harris (2001) estimate the probability of exiting
welfare using longitudinal data from the PSID between 1989 and 1996. Although the
time period is quite short (particularly to measure the impact of policy changes that


Discussions with staffers at HHS suggest that the primary problem is likely to be that entries are
undercounted. In particular, in many states a woman who has recently been on welfare and who returns to
the rolls appears not to be counted among the new entrants.


largely occurred in 1994 and 1995) they find significant effects of waivers, particularly
on the probability of exiting AFDC to work.47
Further work focusing on the underlying dynamics of caseload changes would be
useful. This will require the creation of new and better flow data. In particular, it would
be highly interesting to be able to estimate the impact of specific policy choices on entry
and exit rates within states.
The Effects of Policy Components. A number of the econometric investigations of
caseload changes attempt to measure the impact of specific policy components. That is,
these studies go beyond simple dummy variables that code the implementation of any
waiver or any TANF plan and try to code the specific nature of the policy change.
Because the available data on state policies is limited, these studies typically limit
themselves to looking at 6 or 7 specific policies.48 For instance, one might code when a
state enacted time limits (some states received waivers to do this, some states enacted
them as part of their TANF plan, some states have no time limits but have declared they
will continue funding families out of state funds after 60 months).
On the one hand, this literature goes inside the “black box” of policy changes and
does not treat “welfare reform” as a single variable. On the other hand, efforts to analyze
the effects of specific policies have at least two major problems. First, only a partial set
of policies are typically analyzed. For instance, if states that implement lower benefit

This paper utilizes relatively simple duration models. A companion paper (2002) looks at recidivism
(returns to AFDC) among AFDC leavers. But given the short time frame in which to observe the effects of
policies enacted in 1994-95 on recidivism, it is not surprising that there are few significant effects estimated
for waivers.
Most typically, policy coding includes the implementation of time limits, a family cap, benefit reduction
rates, age-of-child work exemptions, the timing of work requirements, sanctions and benefit reduction
rates. Not included in any of these studies is information on diversion policies, the nature of jobpreparation activities, or the availability of child care subsidies or other work supports. Of course if the


reduction rates also provide more generous child support to those who go to work, then
including one policy (BRRs) without the other (child support supplements) will produce a
biased estimate. An example is found in Kaushal and Kaestner (2001) whose only policy
variables are measures of time limits and family caps. This has the effect of attributing
all of the effects of welfare reform to these two variables. Second, the number of states
that have implemented specific policies is very limited in many of these studies. Many
studies use data only through 1996, which allows them to code the policy specifics of
waivers only. Few enough states received waivers for specific policies that there is a
fundamental lack of identification in many of these studies. Evidence of this is seen in
the regular occurance of perverse signs on some of these policy variables.49
Among the studies that look at policy specific effects are CEA (1997, 1999),
Ziliak, et. al. (2000), Moffitt (1999), Schiller (1999), and Kaushal and Kaestner (2001).
(For more information on these studies, see Table 6.) It is hard to produce a summary set
of conclusions for this work. With different specifications and slightly different data
periods, different studies get different results on quite similar variables. Not all of these
results make sense, for instance, CEA (1999) finds that family caps increase caseloads;
Ziliak, et. al. (2000) finds that strong work incentives increase caseloads. It is difficult to
draw strong conclusions about the impact of specific policies from this literature.
Three papers are somewhat more persuasive. Grogger (2000) notes that families
with younger children should be more affected by time limits, since they are more likely
to be constrained by such limits. He interacts the adoption of state time limits with age of

implementation of these other (nonincluded) policies are correlated with the implementation of some of the
included policies, this can bias the measured effects.
Most of the specific variables also end up being insignificant in most of the estimates. Of course, this is
consistent with a lack of identification, but it is also consistent with a lack of policy effects.


youngest child in the family and finds consistently greater and more negative effects of
time limits on families with younger children. He estimates that 12 percent of the
decline in welfare caseloads in the mid 1990s might be due to time limits. Even this
paper, however, should be read with some skepticism since there are omitted policies that
might be correlated with time limits. Grogger (forthcoming) extends this work, showing
that time limits also increased work more among women with young children and
Grogger (2002) indicates the effect occurs in other data sets.
Hofferth, Stanhope, and Harris (2001) investigate the effects of specific waiver
policies, using data from 1989-96 from the Panel Survey of Income Dynamics to look at
welfare exits. While their results on the determinants of “any exit from welfare” result in
largely insignificant coefficients on specific policies, their results on the determinants of
“exit from welfare that results in work” are more conclusive. They find that stricter work
requirements and fewer exemptions for mothers with young children are positively
correlated with welfare-to-work exits, while lower benefit reduction rates are negatively
correlated. The lack of a complete set of welfare-related policies causes omitted variable
problems with this study as well.
There is still much room for further research that uncovers the effects of specific
policies through controlled estimation techniques. It would be helpful to have a fuller
specification of state policies, longer time periods to observe the full effect of these
policies (especially in the post-TANF era), variation in policy within states over time to
provide stronger identification of effects, and better ways to identify the effects of these
policies on the groups which they most impact. Experimental evidence on the effect of a
few specific policy choices is discussed in Section VIII below.


Food Stamp Caseloads. While most of the literature has focused on
AFDC/TANF caseloads, one might also be concerned about access to other means-tested
programs as well. As women leave cash public assistance programs for work, they
should maintain their Food Stamp eligibility if their overall incomes remain low. Hence,
rapid declines in Food Stamp caseloads in the mid 1990s were viewed with concern by
Food Stamp caseloads have tracked AFDC caseloads quite closely since the late
1970s. This is not surprisingly, since over 80 percent of AFDC recipients also received
Food Stamps (U.S. House of Representatives, 2000, Table 15-3). Although Food Stamps
have been historically available to all low-income families and individuals, take-up rates
have been quite low among the non-elderly, non-AFDC population.50 This suggests the
historical importance of AFDC as a “gateway” program into Food Stamps.
Like AFDC, Food Stamp caseloads increased from 1990-94, peaked in 1994, and
then began to decline rapidly. They fell 37.5 percent from 1994-2000. While their rate
of decline was similar to the decline in AFDC/TANF in the 1994-98 period, it began to
slow and Food Stamps fell much less in 1998-2000 than did TANF caseloads.
Despite the expectation that many families should maintain Food Stamp
eligibility, Zedlewski (2001) indicates that almost two-thirds of welfare leavers leave
Food Stamps as well. Even among very low income families leaving welfare (i.e., those
whose income is below 50 percent of the poverty line), only about half continue to
receive Food Stamps although all of these families should still be eligible. Schirm (2001)


Ohls and Beebout (1993, Table III.1).


indicates that there has been a clear decline in Food Stamp take-up rates among eligibles,
from 71 percent in 1994 to 59 percent in 1998.51
There have been few econometric studies of Food Stamp declines. Wallace and
Blank (1999) estimate Food Stamp caseload determinants, using a model identical to that
which they use with AFDC/TANF determinants. They find Food Stamp caseloads are
slightly more responsive to economic cycles (a one-point rise in the unemployment rate
results in a 6-7 percent increase in Food Stamp caseloads). Waivers appear to have a
significant negative effect on Food Stamp caseloads, although there are typically few
provisions in these waivers directly related to Food Stamps. Similar results are found in
Wilde, et. al. (2000), who look at transitions on and off Food Stamps in the early 1990s
and find strong economic responsiveness and an effect of state welfare waivers. Currie
and Grogger (2001) use post-1996 data and indicate that waivers and TANF both
decreased the food stamp caseload. Figlio, Gundersen, and Ziliak (2000) find significant
cyclicality in the Food Stamp caseload. As with related work on cash benefits, once they
include a lagged dependent variable and various lags in other variables, they find much
smaller effects of policy changes.
More work indicating how Food Stamp caseloads are changing within different
populations can be important. The 1996 legislation limited Food Stamp eligibility among
able-bodied persons without children and the effect of these restrictions would be
interesting to study. Similarly, there has been a sharp decline in Food Stamp use among


This raises a variety of policy-related issues about how families learn of their Food Stamp eligibility and
how they maintain benefits while working. See Greenstein and Guyer (2001) for a review of these issues.


legal immigrant families and their children since the 1996 legislation eliminated their
eligibility. The effects of this change could also be studied.52


Labor Force Participation

Declining caseloads are a mixed indicator. They indicate less receipt of cash
assistance, which is good for those concerned with government budgets but may be bad
from the viewpoint of individual well-being. The thrust of the 1990s reforms was to
increase work and it is important to explore not just whether policies caused women to
leave welfare, but also whether these same policies helped women enter the labor force
and replace their public assistance income with earnings.
The leavers’ studies focus on employment behavior among ex-welfare recipients.
As noted above, this is only a subgroup of those affected by welfare reform (others
choose never to come onto welfare as a result of the reforms). But labor market
opportunities for this group have received substantial public attention. The evidence
suggests that close to two-thirds of welfare leavers are working at a future point in time.53
An even higher share held at least one job since leaving welfare. Martinson (2000) notes
that only 20 percent of leavers appear to never work in a four year follow-up of work
programs in six sites. In short, most leavers find jobs, although jobs and jobholding may
be unstable, so that leavers may not work continuously.54


Borjas (2001b) has a recent paper on this.
Cancian, et. al. (1999) uses the two-thirds number to summarize existing leavers studies. Loprest (2001)
indicates 61 to 64 percent are working at a survey point within two years of leaving welfare. Moffitt and
Roff (2000) cite 63 percent working in studies of three major metropolitan areas. Devere (2001) indicates
55 to 64 percent are working within 3 months of leaving welfare, based on a review of state leavers studies.
A growing body of research has focussed on the effects of personal barriers – such as health problems,
substance abuse problems, low skills, or domestic violence – on work, indicating that mothers with
multiple barriers work less (Danziger, et. al., 2000; Zedlewski and Loprest, 2001).


Wages among leavers vary by study, but typically range between $5.50 and $8.50
per hour among those who are working.55 Most leavers appear to have no more than two
spells of employment inside 4 years (Martinson, 2000), which does suggest job churning
is not extensive. Holzer, Stoll, and Wissoker (2001) indicate that employers rate welfare
recipients as performing as well or better than other employees.
While descriptively interesting, these studies raise a variety of questions. First,
how much did policy influence labor market changes? Second, how did the labor market
respond to this influx of low-wage workers? I summarize the research on each of these
questions next.
Did Policy Influence Work Behavior? Figure 4 indicates that work among single
mothers started to rise in the mid-1990s, strongly suggesting that policy was important to
this change. Other more controlled evidence supports this conclusion.
Moffitt (1999a) and Schoeni and Blank (2000) investigate the effects of waivers
on labor force participation and weeks and hours of work. Both conclude that waivers
had a significant and positive impact on work behavior among less-skilled women. In
contrast, Schoeni and Blank (2000) find few effects of TANF implementation on
increasing labor market participation; once they control for state unemployment and
income changes, the post-1996 rise in labor force participation among less-skilled women
is fully explained. Using a slightly different data set and empirical techniques O’Neill
and Hill (2001) find that both economy and policy matter in the post-TANF era.56


Devere (2001) cites these numbers in summarizing a large number of state leaver studies. Loprest’s
(2001) national survey of leavers finds average wages of $7.15 among those who left welfare between 1997
and 1999. Moffitt and Roff (2000) cite average wages of $7.50. Cancian, et. al. (1999) cite $6.50-$7.50 as
the typical wage range of leavers.
The lack of time fixed effects in the O’Neill and Hill study almost surely results in a larger coefficient on
the TANF dummy variable than in other studies.


In short, these regression studies conclude that policy changes appear to have
mattered in the mid-1990s, although the strong labor market unambiguously helped
increase work among less skilled women as well. These studies focus only on welfare
reform, however, and are largely unable to separately identify the effects of larger
national changes in the EITC or the minimum wage.
There is unanimous agreement that the growing EITC increased labor force
participation among single parents. A number of studies, including Eissa and Liebman
(1996), Meyer and Rosenbaum (2001), Blank, Card, and Robins (2000), Ellwood (2000),
and Hotz, Mullin and Scholz (2001), all find that a sizable component of the growth in
labor force participation among single women can be linked to the EITC expansions.57
The lack of studies that effectively include both welfare reforms and EITC changes
makes it difficult to talk about the comparative impact of these two policy changes.
Grogger (forthcoming) is unique in trying to explicitly control for both EITC parameters
and welfare reform effects. He finds significant effects of the EITC on welfare usage and
work behavior as well as significant policy reform effects. Ellwood (2000) argues the
independent effects of the policies cannot be accurately separated because many of the
welfare reforms were administrative in nature and interacted with the strong economy
and the growth of EITC supports.
The minimum wage also rose in both the early and the mid 1990s. While
minimum wage increases should raise the returns to work among low skilled workers,
they might also result in a loss of jobs. Despite a great deal of debate about minimum
wage effects on teenagers, we have far less evidence of minimum wage effects on single


Eissa and Hoynes (1998) indicate that the EITC may have small negative effects on labor force
participation among married women.


mothers. Card and Krueger (1995) summarize the studies on minimum wage effects;
almost all focus on teenage employment. Bernstein and Schmitt (1998) investigate the
minimum wage increases of 1996 and 1997 and conclude there is little evidence of job
loss among adults due to these minimum wage changes. Neumark (2001) finds the
changes affected employment primarily among unskilled teen workers.
Only one paper has addressed the effect of child care subsidy policies under
welfare reform on mothers’ work behavior. Lemke, Witt, and Witte (2001) use data from
Massachusetts to demonstrate that the availability of subsidies and the attributes of the
local child care market both affect the probability a welfare recipient moves into work.
Ideally, one would like to measure the combined effects of all policy changes, as
well as their individual (and potentially interactive) effects. Research that does this is not
available. It does appear, however, that both the welfare reforms and the growing work
support programs of the 1990s contributed to the sharp rise in work among single parents.
A final set of evidence on the impact of welfare reform on labor market
participation comes from the randomized experiments that measure the impact of specific
welfare-to-work efforts on the behavior of the experimental group (the group that
receives the program) versus the control group (the group that does not receive the
program). This evidence is voluminous, with two decades of experiments that analyze
various welfare-to-work efforts. Almost unanimously, these studies indicate a significant
positive effect of welfare-to-work efforts on labor market participation, although the size
of that impact varies across studies and programs (Gueron and Pauly, 1991; Bloom and
Michalopoulos, 2001). I summarize some more recent contributions to this experimental
literature in more detail in Section VIII below.


How Did the Labor Market Respond? The large influx of less-skilled women into
the labor market constitutes a substantial increase in labor supply. A best estimate is that
welfare reform will increase labor supply among less-skilled women by a little over 1
million workers between 1996 and 2002 (Bartik, 2000, Table 2.1). This is a labor supply
shock equal to 3.1 percent of employment among all women with less than a college
An outward shift in the labor supply curve of one group of less-skilled workers
would be expected to lower wages for all less-skilled workers, if the new group is a close
substitute for existing workers. An observer might be particularly worried about how
these labor force participation increases have affected other previously-working lessskilled women. Although the less-skilled male labor force tends to work in a somewhat
different set of occupations and industries (Blank and Schmidt, 2001), there is enough
overlap in jobs that this group should also be affected.58
The raw data suggests that any supply shifts (which would have lowered wages)
were swamped by the overall demand increase due to a booming economy. Wages
among less skilled women rose throughout the 1990s and unemployment rates fell. In
fact, female unemployment rates were at their lowest point in several decades, while
wages among less skilled women were at their highest point in several decades by the end
of the 1990s. As a result, there was little public discussion of displacement issues. Of
course, it is always possible that wages would have risen even faster in the absence of
this supply shift.


Black, McKinnish, and Sanders (forthcoming) show that shocks to wages of low-skilled men affect
levels of welfare receipt.


There is evidence that the rapid labor supply increase among single moms might
have affected other groups. As Figure 4 indicates, labor force participation increases
among married women with children slowed noticeably in the latter part of the 1990s, at
just the time when work among single women with children expanded. Even more
striking, among less-skilled men labor force participation over the 1990s continued to fall
(Holzer and Offner, 2001). This surprised labor economists, who would have predicted
that the strong economy of the 1990s would pull more of these men into the labor force.59
On the other hand, it is hard to believe that men (or women) were deterred from entering
the labor market by increased employment among ex-welfare recipients when overall
unemployment rates were hovering around 4 percent throughout the country and
employers complained constantly about a lack of workers.
Several papers have tried to document who hired ex-welfare recipients. Holzer
and Stoll (2001) analyze survey data from employers in four major cities in 1998 and
1999 and find that three percent of all job openings went to ex-welfare recipients. Lane
and Stevens (2001) use administrative data from Maryland to investigate whether certain
employer characteristics are more likely to result in long-term employment by newlyhired welfare recipients. They find that welfare leavers appear to have significantly
different experiences in different industries, among smaller versus larger employers, and
among shrinking versus growing emplowers.
Bartik (2000, 2001) takes on the displacement issue. He indicates that welfare
reform is unlikely to have large effects on the overall labor market, since the labor supply
shock is too small. He estimates the effect on wages and employment among less-skilled

For instance, Freeman and Rodgers (1999) indicate that falling unemployment strongly increased labor
force participation among young men in metropolitan areas in the mid-1990s, although they could find no


labor market groups using a variety of models and indicates that different estimation
approaches can result in quite different numbers. For instance, estimates of the elasticity
of labor demand to changes in labor supply vary widely across models. Bartik’s
preferred estimates suggest that welfare reform should reduce wages among female high
school dropouts by between 5 and 15 percent.60 Wage effects among other groups are
lower. He forecasts that the effects of welfare reform on wages and employment among
less skilled women will be larger and more visible in the near future.
It is difficult to untangle the effect of changing labor supply when labor demand is
also changing rapidly. Bartik’s estimates suggest that the answer depends very much
upon the model specified. This is a ripe area for further investigation, including a closer
look at why labor supply among less-skilled men did not grow over the 1990s, better
estimates of the labor demand elasticities for less-skilled workers, and attention to the
effects of any future economic slow-down on (more recently hired) ex-welfare recipients
versus other labor market participants.

VII. Income, Poverty and Well-Being
Many would claim that the overall effects of welfare reform should be evaluated
in terms of their net income-increasing or poverty-reducing impacts.61 As we will see,
this is a much less-well understood area of analysis than the analysis of caseload change
or labor force participation.

effects for adult men.
Others who have simulated these effects with simpler models include Bernstein (1997) and Solow
The 1996 legislation itself made no mention of poverty reduction.


In part, this reflects the fundamental problem of appropriately measuring
economic well-being. Cash income is not an adequate concept if many low-income
families receive in-kind benefits. There are serious problems with underreported income
among the low-income population (Edin and Lein, 1997). After-tax income may be a
better measure than before-tax income, particularly in a period when tax rules (especially
the EITC) for low-income families are changing.62 One might want to measure
disposable income and include an accounting for unavoidable transportation or child care
expenses associated with entering the work force. Even better, one might want to look at
consumption rather than income data. Unfortunately, data are not readily available that
provide reliable and consistent information on all of these measures. Even if one focuses
only on changes in income-based poverty or poverty gaps (the two poverty-based
measures that are most often used) there are difficulties in measurement and
interpretation, as discussed in Section III above.
Finally, it is worth noting that many other measures of well-being than income,
poverty, or even consumption might seem useful. One might want to know about quality
of housing, food intake and nutrition, crime victimization, mental health, health insurance
access, or access to good public education. Welfare reforms may change child wellbeing by affecting parental oversight as well as family income.63 Consistent data on
these measures are even less available than are credible income measures.
In this section I summarize what is known about the interaction between welfare
reform and changes in income, poverty, and other measures of well-being. The existing

The Bureau of the Census makes available special Current Population Survey tapes, based on the March
supplement (which includes income and income components for the previous year), that include imputed
in-kind income and taxes.


information described in this section is quite limited. There is a great need for more
research, better data and more comprehensive measurement of well-being changes and
their relationship to the 1996 legislative reforms.
A major premise of the 1996 reform was the claim that work would make people
better off. Those who testified in favor of this legislation presented charts at
Congressional hearings showing that women who worked would be economically better
off than women who stayed on welfare, particularly with the minimum wage and EITC
changes enacted by earlier Congresses (Haskins, 2001). Indeed, a series of simulation
exercises done in the late 1990s showed unambiguously that steady work, even at a
relatively low wage, when combined with the EITC, with child care assistance, with
access to Medicaid, with Food Stamp and Child Support assistance, would leave a
woman substantially better off (Acs, et. al., 1998). Critics claimed that these simulations
were unreliable since many women did not have access to all of these work supports and
many women were not able to find or maintain steady employment. The evidence on
income and poverty (Tables 3 through 5) suggest that most single mothers had higher
incomes by the end of the 1990s, despite a loss in government assistance.
Leavers’ Studies. Few of the studies of ex-welfare recipients contain any
information on overall economic well-being of leavers; most focus only on welfare use
and labor force participation. Haskins (2001) indicates that income among welfare
leavers in these studies must be around $11,000, based on earnings and work information.
Among those studies that calculate poverty rates, most find quite high poverty among
leavers, although the numbers vary widely. For instance, Loprest (2001) uses a national


Grogger, Karoly and Klerman (2002) summarize various studies (mostly state-specific) that present
survey data measuring material well-being among children.


survey of leavers to suggest that 48 percent remain poor. Danziger, et. al. (2001) report
about 50 percent of welfare leavers were poor (based on annual incomes two years after
welfare receipt.) Moffitt and Roff (2000) look at data in three cities and estimate that 74
percent of leavers are poor. Cancian, et. al. (1999) uses data from the NLSY to indicate
that 55 percent of women are poor in the year following an exit from welfare, but this
falls to 42 percent five years later. Bavier (2002) looks at monthly panel data on welfare
leavers from the SIPP and concludes that income rises over time among leavers, in part
because earnings of other family members rise.
Two studies provide some comparisons over time. Loprest (2001) finds evidence
of slight improvements in the percent working and the monthly earnings of women who
left welfare between 1997-99 versus leavers from 1995-97. This should mean that later
leavers had higher incomes, and indeed poverty rates are lower in this group. Cancian,
et. al. (2002), in a study based on Wisconsin data alone, find evidence of lower earnings
among welfare leavers in 1997 versus 1995. Neither of these studies, however, can
control for changes in the composition or selectivity of welfare leavers over time.64
Regression Analysis of Poverty and Income Changes. None of the evidence cited
above attempts to separately identify the causal factors behind income and poverty
changes over the 1990s. Three studies listed in Table 6 have looked at these variables,
using the now-familiar state panel data methodology to estimate the determinants of
changes in family income and poverty probabilities.


I cite no experimental evidence in this section. Most randomized studies of welfare-to-work changes
looked only at earnings and have no information on overall income changes. A few more recent studies of
waivers involving multiple program changes are exceptions to this. Consistent with leaver study results,
these tend to show little change in income (Bloom and Michalopoulos, 2001).


Schoeni and Blank (2000) find that the waivers enacted in the early 1990s
appeared to increase income among low-income women. Moffitt (1999) finds an effect
of waivers on earnings, but their estimated effect on total income is small and poorly
determined.65 Grogger (forthcoming) finds that waivers and TANF reforms increased
both earnings and income. Schoeni and Blank investigate the impact of waivers and
TANF on poverty rates as well as income. They find that the implementation of waivers
is associated with a 2.4 point decline in the poverty rate among less-skilled women,
holding the state economic climate constant. The implementation of TANF is associated
with a 2.0-2.2 point decline in the poverty rate among less-skilled women. This evidence
suggests that the welfare reform policies had income-improving effects for disadvantaged
women.66 Gunderson and Ziliak (2001) investigate the effects of welfare reform on
poverty rates and poverty gaps among different subgroups among the poor and also find
significant effects.
These results, based on national samples of all low income women, are stronger
than those from studies that look only at welfare leavers. This suggests that income
increases among those who don’t enter welfare (that is, the non-entrants who would have
gone on welfare in the pre-reform period but choose to remain off welfare post-reform)
are large. This is precisely what one might expect if non-entrants were self-selected to be
more employable. It is also worth noting that leaver studies typically do not ask about
income or earnings among other family members, which several studies find to be a
major reason why total incomes among single mothers are rising.

Moffitt looks only at single mothers, while Schoeni and Blank look at all women.
Schoeni and Blank try to investigate the effect of these policies across the income distribution and find
that waivers appear to have benefited all women with less than a high school degree. In contrast, TANF


Consistent with these results are estimates by Meyer and Sullivan (2001) who
focus on consumption rather than income among single mothers. They find that total
consumption of single mothers increases in the mid-1990s, both absolutely and relative to
income among women without children and married mothers. (There are a few
subgroups for which this is not true.) They interpret this as evidence that welfare reform
did not harm women’s well-being.67
The well-being of two specific groups deserves mention. Legal immigrants
entering the country after August 1996 were made ineligible for virtually all forms of
federal public assistance (TANF, Food Stamps, Medicaid, or SSI).68 The impact of this
provision is likely to grow over time as a growing share of new immigrants are covered
by it. There has been remarkably little literature studying the impact of these provisions
on the behavior and well-being of the immigrant population. Use of public assistance
among immigrants has fallen much more rapidly than among non-immigrants. For
instance, between 1994 and 1998, the share of immigrants receiving AFDC/TANF or
Food Stamps fell almost in half (Borjas, 2001a, Table 14-2). Food Stamp receipt among
eligible citizen children living with immigrant parents fell from 80 percent in 1994 to 46
percent in 1999.69 Both Lofstrom and Bean (2001) and Haider, et. al. (2001) claim that
the faster declines in immigrant welfare use are largely due to different local labor
markets in high-immigrant versus low-immigrant regions. Kaestner and Kaushal (2001)
suggest that welfare changes have increased employment among more recently-arrived
appears to have benefited only female high school dropouts above the 20th percentile of the income
distribution of all female high school dropouts.
Another closely-related topic is the effect of welfare reform on household savings. Hurst and Ziliak
(2001) provide an analysis of this issue.
At their option, states were allowed to run state-funded programs serving immigrants and a number of
states have taken this option (Borjas, 2001b). California, with the largest immigrant population, is
particularly generous.


immigrants. Further studies looking at the connections between these policy changes and
the changing economic and employment status of immigrants would be very useful.
A second group of concern is children. Duncan and Chase-Lansdale (2001a,
2001b) provide the best available discussion of how child well-being might interact with
welfare reform. Below, I discuss evidence on the impact of financial incentive welfareto-work programs on child well-being. Evidence is limited that relates welfare reform
more broadly with child outcomes. Bennett, Lu and Song (2001) argue that welfare
reform has led to an income decline among families where the parent has less than a high
school degree. Paxson and Waldfogel (forthcoming) indicate that higher rates of out-ofhome placement appear linked with some aspects of welfare reform. Haider, Jacknowitz,
and Schoeni (2001b) show that breastfeeding rates appear lower due to greater work
behavior. This is another area where further research would be highly useful.

VIII. Experimental Evaluations of Specific Policy Choices
While experimental evaluations of welfare reform programs have limitations, as
discussed above, they provide some of the most credible evidence about the effects of
specific reforms. I focus here on a few topics which have been evaluated by random
assignment methodology and that particularly add to our theoretical and empirical
knowledge of the effects of redesigned welfare programs. This section reviews the
evidence on three specific policy choices: Mandatory employment programs, earnings
disregards and financial incentive programs, and time limits.
Mandatory Employment Programs. Since the mid-1980s, states have
experimented with a wide variety of welfare-to-work employment programs. Most of

Underlying data provided by USDA for tables published in USDA (2000).


these have been mandatory, meaning that welfare recipients who are ruled to be “work
eligible” are required to participate if they want to continue receiving welfare benefits.
Summaries of evaluations of earlier welfare-to-work efforts, both mandatory and
voluntary, can be found in Gueron and Pauly (1991) and Friedlander and Burtless (1995).
States that received waivers from AFDC program rules to run strong mandatory
welfare-to-work programs in the early 1990s were also required to fund a serious
evaluation of their new program, typically a random assignment evaluation. As a result
of this, a wide variety of mandatory welfare-to-work programs were evaluated in the
early 1990s. The results from these programs are nicely summarized in Bloom and
Michalopoulos (2001) and in Michalopoulos and Schwartz (2001), both of which review
randomized evaluations of 20 mandatory welfare-to-work programs in specific states.70
Virtually all of these programs produced some significant increases in
employment and reductions in welfare usage and payments. Earnings per year increased
between $200 and $600 in most programs.71 Michalopoulos and Schwartz (2001) break
these results down for different groups of participants. They indicate little difference in
the employment gains experienced by the most versus the least disadvantaged
participants in these programs (which means that the ongoing earnings and employment
differentials between these two groups remained about the same after recipients
participated in mandatory welfare-to-work programs, although both groups worked more
and earned more). It is particularly interesting that employment outcomes did not seem
significantly worse among less skilled participants, or participants with identifiable


See also Hamilton, et. al. (2001) which summarizes information on program effectiveness in a five year
follow-up of 11 welfare-to-work programs.
The largest earnings increase occurred in the Riverside County GAIN program, where annual earnings
gains exceeded $1000/year.


barriers to work, such as child care problems. The one group that appears not to benefit
from these programs are recipients at a high risk of depression.
A key comparison in these studies is between those programs that focused on job
search or labor force attachment (LFA) through some sort of work-first program that
pushed recipients into jobs as rapidly as possible, and those programs that focused on
human capital development (HCD) and provided more training and educational
opportunities to recipients. Three programs included side-by-side evaluations of LFA
versus HCD welfare-to-work programs within the same location (Atlanta, GA, Grand
Rapids, MI, and Riverside County, CA). Other programs had somewhat mixed models,
including work-first efforts for some recipients and education and training for others.
While labor economists are particularly likely to predict that education and
training will make people better off in the long run, the existing evaluations challenge
that assessment. Work-first and LFA programs increased earnings and decreased welfare
usage more quickly, while HCD programs cost more, particularly in the first year when
women were in training rather than working. But even three years out, after women from
HCD programs had been in the labor market for up to two years, HCD participants did
not outperform LFA participants. This may suggest that the gains to experience among
women who have been out of the labor market may be larger than the gains to education
and training, at least initially. While the HCD programs significantly increased the
number of participants holding a GED degree, there was little evidence that this resulted
in higher earnings or more work hours (Freedman, et. al., 2000).
These evaluations had three year follow-up surveys, at the most. Using data from
the California GAIN program, Hotz, Imbens, and Klerman (2000) match control and


treatment group members from earlier welfare-to-work programs in California with
earnings records, allowing them to follow welfare-to-work participants (and their control
groups) for up to nine years afterwards. They find that in years 7-9, those who received
more education or training are doing as well or better than those who were put into workfirst programs. Their conclusion is that the HCD programs look better with longer-term
evaluations. This study uses data from one state only, and verifying these results for
other programs would be useful.
Interestingly, the best results from these studies occur in programs with mixed
activities, suggesting that a combination of work-first for some women and education for
others might be optimal. For instance, the Portland, OR, program and the GAIN program
in Butte, CA, for single women showed $1200/year earnings increases, while GAIN
Riverside (CA) showed $1400/year increases (Bloom and Michalopoulos, 2001). Further
experimentation with mixed activity programs would be useful, particularly evaluations
of retention-based programs that provide education, training, or job retention services to
women after they have worked for a period. Anecdotal evidence suggests that many
women who participate in work-first programs appear to recognize the need for further
training at a later date. Some women lose their jobs and have difficulty finding another
job. Second-chance programs would aim at assisting job retention or providing training
after a woman has acquired some labor market experience. No programs of this sort for
women moving from welfare to work have been evaluated with randomized experimental
A disappointing aspect of the mandatory work programs is that they provide little
evidence of increased income. In fact, increases in earnings appear to be entirely offset


by losses in public assistance income.72 Hence, these programs have no anti-poverty
effects. This has led to a great deal of interest in the use of earnings disregards in
conjunction with mandatory work, to create work incentives and subsidize earnings at the
same time.
Earnings Disregards and Financial Incentive Programs. Several studies have
tested the effects of strong earnings supplements as a way to incentivize work and reduce
welfare usage. These so-called “financial incentive programs” include the Minnesota
Family Investment Program (MFIP) (Miller, et. al., 2000, and Gennetian and Miller,
2000), the New York Child Assistance (CAP) program (DeMarco and Mills, 2000), the
New Hope program in Milwaukee (Bos, et. al., 1999), the Work Restructuring Project
(WRP) in Vermont (Bloom, et. al., 1998), and the Self-Sufficiency Project (SSP) in
Canada (Michalopoulos, et. al., 2000). Two of these programs – MFIP and SSP -- have
explicitly tested the combined versus separate effects of earnings disregards and other
employment service programs. Three other programs have been evaluated that included
financial incentives along with other policies: the Connecticut Jobs First program
(Bloom, et. al., 2000b), the Florida Family Transition Program (FTP) (Bloom, et. al.,
2000a), and the Iowa Family Investment Program (FIP) (Fraker and Jacobson, 2000). In
these three evaluations it is difficult to make statements about the effect of financial
incentives only, but they do show the combined effects of financial incentives along with
a mix of other mandatory and voluntarily-available job search services. Table 7 shows


These results are typically based on administrative data on earnings and benefits. Cancian, et. al. (1999)
indicates that this is likely to undercount true family income since it does not include income from partners
or other family members.


the effects of these programs on a set of key variables, as measured by random
assignment evaluations.73
Because of their strong evaluation results, both MFIP and SSP have garnered a
great deal of interest and I describe them briefly to the reader. MFIP was implemented in
Minnesota in 1994, and provided a strong earnings disregard that allowed women to
receive some cash assistance until their earnings were about 140 percent of the poverty
line.74 Participants were also required to participate in mandatory job search programs.
A subset of the treatment group was provided with the financial incentives from earnings
disregards, but not subject to mandatory job search requirements. A control group
continued to receive AFDC. Participants were randomized into both treatment groups
and the control group, so that the separate effects of mandatory job search and earnings
disregards could be explored.
The SSP program was implemented in 1992 in two provinces in Canada (New
Brunswick and British Columbia).75 It offered a randomly chosen group of women on
welfare (known as Income Assistance in Canada) an alternative: If they agreed to leave
welfare, they could receive an earnings supplement in every month when they averaged
30 hours of work per week or more. The supplement was large and roughly doubled the
earnings of most participants. It was calculated as half the difference between a
participant’s earnings and an “earnings benchmark”, set at $30,000 in New Brunswick
and $37,000 in British Columbia (Canadian dollars). The supplement was reduced by 50

For a more thorough discussion of the results of financial incentive programs see Blank, Card, and
Robbins (2000) or Michalopoulos and Berlin (2001).
For more detailed description of the MFIP program, see Miller, et. al. (2000).
For more information on the SSP project, see Michalopoulos, et. al. (2000) or Quets, et. al. (1999). Note
that the SSP experiment offered women a choice, hence some of the treatment group chose to stay in
Income Assistance. In contrast, those in MFIP’s treatment group had to participate in the alternative
program and were no longer eligible for AFDC.


cents for every dollar of earnings. Some of these women were also randomly assigned to
an SSP-Plus program, which combined the earnings supplement with job-related services
such as resume writing assistance, job search assistance, and self-esteem workshops.
Participation in these services was not mandatory, so the evaluation compares the effect
of earnings supplements with and without voluntary employment services.
The results of the earnings disregard experiments suggest that positive work
incentives coming through larger earnings disregards can increase employment. The top
part of Table 7 indicates that employment increased by 3.6 percent among those receiving
MFIP financial incentives only, and by 3.3 percent in the New York CAP program. The
relatively small financial incentives in the Vermont WRP program led to almost no
employment effects.
As discussed above, mandatory employment programs alone appear to have little
effect on income or poverty, but Table 7 indicates that the MFIP incentive-based program
had significant positive effects on monthly income and significant negative effects on
poverty (although WRP and CAP did not.) In the MFIP incentives program, this was
entirely due to the earnings benefit supplements; earnings actually decreased slightly.
This highlights the fact that earnings disregard programs cost more, since they pay
benefits to supplement earnings of workers, phasing out more slowly than less-generous
welfare programs. Hence, these programs tended not to reduce the cost or the usage of
welfare assistance. They significantly increased the amount of assistance that went to
workers, however, rather than non-workers.
Most promising of all were the programs that combined employment programs
with earnings disregards, shown in the bottom half of Table 7. The SSP earnings


supplement required working 30 hours per week and provided the largest financial
incentive to work among these programs. The result was a 7.2 percent employment gain
among those offered the SPP program, significant income increases, and a greater than 9
percent decline in poverty rates.76 The full MFIP program that included both generous
disregards and mandatory employment programs had large positive effects on
employment and income, and significant negative effects on poverty. This was due to
both significant earnings increases combined with significant ongoing cash transfers to
the workers.77 The MFIP evaluation allows us to measure the separate impact of
disregards versus mandatory employment; the results indicate that the significant
employment effects depended upon the mandatory employment program, while the antipoverty effects depended upon the high earnings disregard.
Other programs that combined both financial incentives and strong work
requirements show similar gains in both employment and in income. As Table 7
indicates, the Connecticut Jobs First program and the Vermont Welfare Restructuring
Program resulted in strong earnings and employment gains, and (smaller) income gains.
The Florida FTP program and the Iowa FIP programs have limited earnings disregards,
but these are large enough that the loss of cash transfers is less than the earnings gains,
hence women in these programs also increased employment and increased earnings.
Again, these results are a sharp contrast to the mandatory employment programs alone,
where earnings gains are typically entirely offset by cash transfer losses.

Card, Michalopoulos, and Robins (2001) also describe earnings gains among SSP recipients of around
2.4 to 3 percent per year over the period of the experiment. It is also worth noting that a substantial number
of persons who were offered the SSP supplement did not take it up. Most of these non-participants said
that they would have liked to receive the supplement but could not find full-time work or could not
overcome various barriers to work.
The 30 hour work requirement in SPP resulted in a substantial rise in full-time work. In contrast, MFIP
had more of an effect on part-time work.


The evidence in Table 7 is striking and worth emphasis. In traditional welfare
programs (see Figure 2), maximum benefits are paid to non-workers. Hence, traditional
welfare programs typically increase income but reduce labor supply at the same time,
creating inefficiencies. Burtless (1986) notes that in the Negative Income Tax
experiments, the government had to spend almost $2 to increase incomes by $1, largely
because of labor supply reductions. In contrast, financial incentives programs (especially
those with mandatory employment programs) provided strong work incentives at the
same time they supplemented incomes. In these programs, both labor supply and income
Part I of Table 8 presents calculations of income gains per dollar spent for some
of the financial incentive programs that included both incentives and work requirements.
Column 1 shows income gains to program participants and column 2 shows transfer
payments. Column 3 indicates the income gains per dollar transferred. An alternative
calculation occurs in column 6 which shows total program benefits (column 4, including
such things as the imputed value of additional health care) per dollar of total program
costs (column 5, transfers plus the provision of other services and administration). In
looking at Table 8, one might be tempted to think that programs with a benefit/cost ratio
of less than one should not be run. I caution against this interpretation. In many cases
programs with lower benefit/cost ratios may offer important and necessary services.
Programs with higher benefit/cost ratios are relatively more appealing, but the data in
Table 8 do not allow one to drawing any absolute conclusions about the value of these


In the SSP program, $1 in government transfers increased income by almost $2
among long-term welfare recipients since the earnings supplements were reinforced by
increased labor supply. In MFIP (among long-term recipients) the gain is even larger
and $1 in government transfers increased income by almost $2.50; New Hope also shows
substantial gains. Only two-parent families in MFIP show relatively small gains for each
dollar transferred. This suggests that these financial incentive programs are relatively
efficient in redistributing income. Even in column 6, where the calculation is based on
total program costs, the ratios are better than the 0.50 number cited by Burtless for the
negative income tax (again the exception is among two-parent families in MFIP.)78
In contrast, the mandatory employment programs summarized in part II of Table
8 show much smaller benefit gains in absolute terms (column 4) and generally lower
income gains per dollar of government spending (column 6). In some cases, there are
actual income losses among recipients, resulting in negative ratios. As redistributive
programs, these are simply less effective. These mandatory employment programs were
generally not focused on income gains, so it may be unfair to judge them on this basis. In
fact, a primary goal of most of these programs was to reduce government spending, and
many of them were quite effective at that. Some of these programs, such as Riverside
GAIN, even saved the government substantial amounts of money per recipient; while
income gains were small in Riverside, the government savings suggests a very efficient
transfer program.
In addition to their income-enhancing effects for the family and their
employment-enhancing effects for the parent, financial incentive programs also appeared


The calculations in columns 4, 5, and 6 require more imputations and assumptions and hence may be
regarded as slightly less reliable than those in columns 1, 2, and 3.


to have positive effects on children’s outcomes. A number of these studies have
collected data on child outcomes as well as on employment and income. Morris, et. al.
(2001) summarize this research and indicate that earnings supplement programs (alone or
combined with mandatory employment programs) appear to have significant and positive
effects on school achievement and child behaviors among elementary-school-age
children.79 Mandatory employment programs alone do not appear to produce these gains.
These effects are strongest among the children of long-term welfare recipients. Duncan
and Chase-Lansdale (2001a) suggest that these changes appear to be operating through
changes in the utilization of child care or after-school programs, rather than through
changes in home environments.
Adolescent effects are based on smaller samples and are less positive. Two
studies find reductions in achievement and increases in behavioral problems among teens
whose mothers participate in work incentive programs.
The evidence that financial incentive programs can reduce poverty, increase
earnings, and may even improve child outcomes at the same time, particularly when
combined with other job-related services, suggest that these financial incentive programs
are the most promising avenue of policy change to come out of the U.S. (and Canadian)
welfare reforms of the mid-1990s. Several caveats about these results should be noted,
however. First, these financial incentive programs have not been run in a random set of
states. The strongest results come from Minnesota and Canada, and might not be
generalizable to other locations. Second, the wide variance in results shown in Table 8
suggests that financial incentive programs are more effective with some populations.


Samples in these studies are too small to produce reliable conclusions regarding the effects on children
under age 3. For an earlier summary of the literature see Hamilton, et. al. (2000).


Time Limits. The effects of time limits have been studied both by randomized
experiments and through larger econometric studies of national data. It is fair to say,
however, that we lack a great deal of information about the effect of time limits, largely
because not enough time has passed to evaluate them. By mid-2000, only about 60,000
families had hit time limits of one sort or another. Only in late 2001 and early 2002 will
the first group of women who were continuously on welfare since TANF was enacted
begin to hit the 60-month time limit set in many states. As more and more families hit
the five-year time limits over the near future, there will be more opportunities to study the
effects of these time limits.
Six state programs that implemented time limits earlier (through state waiver
programs) have been studied through random assignment experiments (Arizona,
Connecticut, Delaware, Florida, Indiana and Virginia). In none of these states do time
limits show large effects on employment, though there is some evidence that women are
leaving welfare early in order to preserve welfare eligibility in the future.80
These results are somewhat difficult to interpret, however. These experiments
were conducted on the very first group of women anywhere in the United States to hit
time limits. This group may be more prone to misunderstand the implications of time
limits or to disbelieve that they would actually be enforced. Furthermore, all of these
experiments are studying of a larger set of changes, which include time limits as one
component. In none of these studies can the independent effects of time limits be
deduced. Conclusions about the effect of time limits on employment are largely based on
comparisons between the results in these states to experimental results in other states


without time limits. In addition, none of these evaluations can investigate the entry
effects of time limits, that is, the extent to which they discourage families from receiving
welfare in the first place.
The effects of time limits on families are an issue of great interest and scrutiny.
Some evidence indicates that a high share of clients who are subject to future time limits
do not entirely understand this provision. The evidence from Florida suggests that the
most disadvantaged were the least affected by Florida’s time-limited program; it had few
effects on their employment, earnings or income (Bloom, et. al., 2000a). Those who hit
the time limit in Florida were clearly struggling financially, but were not notably worse
off than many other families who left welfare for other reasons. Time limits in Florida
did appear to reduce welfare use the most among families with younger children
(Grogger and Michalopoulos, 1999). Those who are “sanctioned off” welfare may be
similar to those who hit time limits. Leavers’ studies indicate that those who leave
welfare due to sanctions are less likely to be employed after leaving welfare and are also
more disadvantaged than other leavers across a range of attributes (U.S. General
Accounting Office, 2000). Lack of long follow-up periods in many of these studies
makes it difficult to evaluate the long-term effects of time limits or sanctions.

IX. Marriage and Fertility Changes
A major impetus for welfare reform within the U.S. has been ongoing concern
about rises in out-of-wedlock births and declining marriage rates, especially among low


See Bloom (1999), Bloom and Michalopoulos (2001) and Pavetti and Bloom (2001) for summaries of
CN, DE, FL and VA studies and references to the original experimental results. The AZ and IN
experiments are described in Fein, et. al. (1998) and Kornfeld, et. al. (1999), respectively.


income women and men. Indeed, the major stated goals of the 1996 legislation included
reducing out-of-wedlock births and increasing marriage.
There are several mechanisms by which welfare reform might accomplish this. A
simple economic model would suggest that means-tested transfer programs make it easier
for lower-income couples to afford a child. Furthermore, the fact that most of this
support has historically been focused on single mothers and not married couples means
that the incentives to marry are limited. While changes in cash assistance programs made
assistance to two-parent couples more available in the early 1990s81, growth in the EITC
increased the marriage penalty for low-income workers (Ellwood, 2000).
In addition to standard economic incentive-based models, there are also a host of
more cultural/behavioral models that claim the growth in out-of-wedlock childbearing is
due to decreased social disapproval of out-of-wedlock childbearing and a shift in
behavioral norms away from marriage. Increases in means-tested support would make it
easier for such shifts in marital and fertility norms to occur.82
Both of these theoretical approaches imply that recent U.S. changes in public
assistance should have reduced the incentives to become a single mother and increased
the incentives to marry. Time limits, sanctions, diversion activities, and work incentives
all make it harder to receive public assistance as a single mother without also engaging in
work-related activities.
Some states have gone beyond these welfare reforms to enact programs that are
explicitly directed at fertility and marriage decision-making. For instance, some state

The Family Support Act of 1988 required all states to make two-parent married couple families eligible
for AFDC (although in most cases these families faced more stringent eligibility requirements).


waivers in the early 1990s allowed states to mandate that teen mothers must stay in
school and live at home with their parents (or in another supervised setting) if they are to
receive cash assistance, the so-called “minor parent provision.” Other states were given
authority to enact “family caps”, which refuse benefit increases to welfare recipients who
have further children outside of marriage. After states received greater discretion under
TANF, more states implemented these programs.83
Trends in the data. Is there evidence of changes in fertility or marital behavior in
the mid-1990s, similar to the labor force participation changes discussed above? Figure 5
shows the trends in three key variables.84 Marriage rates have fallen steadily for many
decades, with no noticeable break in trend over the 1990s. Similarly, divorce rates are
also slowly falling, with no change in the 1990s. Birth rates to unmarried women did
change noticeably around 1990, ending a steep increase to flatten out and even fall
slightly over the 1990s. This change in the nonmarital birth rate is evident among both
black and white women, and among teens and older women, but occurs well before major
welfare reforms were implemented.
Further evidence on trends in key family structural variables can be seen by
looking at the share of families with children that are headed by never-married females.85
This number has increased steadily from 3 percent in 1976 to over 10 percent in 2000, the
highest level ever recorded. When one looks at the trends in headship among nevermarried mothers who have lower incomes or are less educated, however, there is a bit
more evidence that the increases of the past two decades slowed somewhat in the mid-to82

For instance, Murray (1994) argues that the growth in means-tested benefits in the late 1960s/early 1970s
led to long-term increases in out-of-wedlock childbearing. For a discussion of these behavioral arguments,
see Murray (2001).
Maynard, et. al. (1998) discuss these state policies in more detail.


late 1990s. Other recent evidence suggests that the share of children living with single
mothers (particularly in African American families) declined significantly in the late
1990s (Dupree and Primus, 2001). This is at least consistent with the theory that welfare
reform might be producing some behavioral changes among less skilled women.
It might be unreasonable to expect any marriage or fertility effects from welfare
reform to show up within a few years. Only a relatively small share of the population
gets pregnant or becomes married in any given year; changes in these decisions will
affect aggregate numbers only slowly over time. Furthermore, marriage and fertility
patterns may be much more sluggish and resistant to change than is work behavior. All
of this suggests that identifying effects on family structure due to welfare reform is likely
to be difficult, and any measured effects are likely to be small.
Causal analysis of these changes. The literature that relates the policy changes
of the 1990s to changes in marital or fertility behavior is still quite limited and much
good research remains to be done. A large body of earlier work has analyzed the
relationship between AFDC benefits and fertility behavior. I do not review this literature
here, in part because it has been well reviewed elsewhere (Moffitt, 1992; Moffitt, 1998b).
The primary conclusion is that studies tend to show either no effects or small effects. To
cite Moffitt (1998a, p5) in the introduction to a book analyzing the relationship between
welfare and fertility behavior, “[I]t is also fair to note that if there were a sizable effect of
welfare on demographic behavior, it would probably be more evident with the available
statistical methods than appears to be the case in the research literature. The findings


For a discussion of related trends see Murray (2001) or Bachrach (1998).
Author’s tabulations on the March Current Population Survey data from 1976 to 2000.


reported in the chapters are…consistent with the existence of a small, real effect but one
that is difficult to detect and sensitive to the methodology used[.]”
Evidence of small effects in the existing literature do not imply that recent welfare
reform effects must also be small, for at least two reasons. First, this previous literature
focuses on the effect of differences in welfare benefit levels on fertility patterns. As
discussed above, welfare benefit levels have not changed radically; rather, a host of other
behavioral incentives and mandates have been imposed on welfare recipients. These
might have different and stronger effects, particularly if these changes seriously limit
welfare benefit availability. Second, programs like family caps and minor parent
provisions are directly aimed at changing fertility behavior and might have larger and
more direct effects than changes in benefits or availability.86
Table 9 summarizes the literature that attempts to link welfare reform with
changes in family structure. Part A lists the econometric studies. Horvath-Rose and
Peters (2001) use state panel data to investigate out-of-wedlock birth trends from 1984 to
1996, including controls for the implementation of family caps or minor parent
provisions. They find a significant and negative effect of family caps, similar to the New
Jersey study. The minor parent provision appears to have positive effects on nonmarital
fertility in their study, however, which is not the expected sign and suggests that there
may be omitted variable problems with the entire study. Clearly, the mixed evidence on
family caps suggests that further investigation might be useful. Schoeni and Blank
(2000) use panel data to investigate the effects of waivers and of TANF implementation
on the percent married and the probability of being a female household head. They find


evidence that the policy reforms had small but significant effects on these family
formation variables. Fitzgerald and Ribar (2001) use data from the early 1990s and find
state waivers had mixed results on female headship.
Part B of Table 9 summarizes econometric studies that have tried to investigate
the expected effect of family caps using data from the AFDC program. Fairlee and
London (1997) look at whether differences in AFDC benefit levels change the likelihood
that single mothers would have additional births. They find little evidence of this. Acs
(1996) and Grogger and Bronars (2001) have similar results. Argys, Averett and Rees
(2000) investigate how AFDC benefits might affect pregnancy and abortion behavior.
They find small effects that are highly sensitive to specification and methodology.
Experimental evaluations of the effects of employment programs on marriage and
fertility behavior (summarized in Part C of Table 9) show quite mixed results, from what
are admittedly quite a different group of programs.87 Three studies directly analyze
actual family cap programs, each using quite different methodologies. Camasso, et. al.
(1998a, 1998b) report on a pre-post data comparison and an experimental comparison in
New Jersey after family caps were implemented and indicate that the birth rate was
significantly lower among those subject to family caps. Some have raised concerns about
the interpretability of these evaluations, however (Maynard, et. al., 1998). The A Better
Chance (ABC) program in Delaware ran a strong mandatory work activities program and
included a family cap. A randomized study of the program showed few effects on
marriage or fertility (Fein, 1999).

This might be especially true if one takes the behavioral norms model seriously. The implementation of
family caps in most states occurred simultaneously with a lot of media attention to the fact that the state
wanted to actively discourage additional out-of-wedlock births.


The New Chance experiment, which provided educational and job assistance to
teen welfare mothers (along with family planning counseling) found pregnancy rates in
the experimental group actually increased in a randomized evaluation (Quint, Bos, and
Polit, 1997). The Teen Parent Demonstration (TPD) Project in Ohio, which required teen
welfare mothers to participate in a rich set of education and work support programs, had
no effect on second pregnancies (Kisker, Rangarajan and Boller, 1998). The California
Work Pays Demonstration (Hu, 2000) was a work-oriented welfare reform that increased
marriage rates in some populations.
The largest and most positive effect of welfare reform on family structure is found
in the MFIP demonstration, discussed above as a particularly effective financial incentive
program (Miller, et. al., 2000). Single mothers who were in the MFIP experimental
group married at a significantly higher rate than those in the control group, while twoparent families in MFIP stayed married at a higher rate.88
Overall, the recent literature on the effects of policy on family structure has not
provided clear guidance as to what states should do if they want to influence fertility and
marriage through their welfare reform efforts. While the MFIP results are cited as
evidence that welfare reform can influence marriage, it would be useful to have
additional experimental evidence that showed similarly strong and positive results on
marriage or fertility from other state reform efforts. Even some programs that explicitly
focused on fertility issues as one component of welfare reform (such as New Chance or
the TDP program) did not show the desired effects. In addition, further econometric

Murray (2001) also reviews the studies cited here, as well as several others that are not based on recent
welfare reform efforts.


exploration of the determinants of marriage and fertility trends, particularly focusing on
the changes in the 1990s, would be highly interesting.



The U.S. welfare reforms of the 1990s have generated extensive interest. Both
the federal changes in work support programs like the EITC and the revolution in the
design of state public assistance programs have drawn research attention. While it is far
too early to draw any final conclusions about the long-term effects of these program
changes, the research literature to date has produced several important results.
More significant caseload declines and larger increases in labor force participation
among less-skilled mothers were possible than many observers would have predicted.
Entry into welfare fell and exits from welfare rose. There remains debate as to how much
these results were due to a strong economy, to program reform, or to their interactive
effects. While some of this change in behavior is due to traditional labor supply
responses to growing wages and increased financial incentives to work, the changes were
greater than historical experience would lead one to expect. State welfare programs were
substantially different post-1996, including such elements as time limits, sanctions, and
diversion efforts. Tracking down the exact relationship between these program
differences and specific behavioral changes remains difficult, but there is a growing body
of evidence indicating that these new program elements mattered.


Another financial incentive program discussed above, SSP (implemented in Canada), had more mixed
results on marriage. Positive marriage effects occurred in one of the two sites, while the other site showed
negative marriage effects. Harknett and Gennetian (2001) discuss possible reasons for this.


At least over the late 1990s, these changes in behavior occurred along with
moderate increases in cash income and moderate declines in poverty among less-skilled
single mother families, those most affected by the policy changes. This is in contrast to
the mandatory employment programs of an earlier era, which increased labor supply but
seemed to have few positive effects on income (earnings gains offset benefits losses).
These positive outcomes were best demonstrated in a set of experimental evaluations of
so-called “financial incentive programs” which both provided financial incentives to
work while also mandating strong work efforts. These programs, enacted in only a
limited number of states, seem to have been particularly effective in increasing
employment and reducing poverty, and they provide perhaps the best model of “newstyle” welfare programs. Their results are markedly different from those of the older
negative income tax experiments.
The literature evaluating these welfare reforms is likely to continue to grow. Let
me mention three key areas where future research may be particularly important. First,
some important questions can only be answered after more time has passed. We have
only very preliminary evidence on whether these reforms have had any long-term impacts
on marriage or fertility behavior. Similarly, we are just at the beginning of observing the
impact of actually imposing time limits on larger numbers of welfare recipients. Most
important, perhaps, is the question of how much the remarkable U.S. economy in the late
1990s was fueling the declines in caseloads, and increases in work and income among
low-wage single mothers. Only as we experience economic cycles will we be able to
effectively separate the economic effects from the policy effects of welfare reform.
Tracking the changes in a less-robust economy will be important, as will investigating


whether certain states have packages of programs that make their low-income citizens
more or less vulnerable in an economic downturn.
Second, the well-being effects of these policy changes should be better
understood. We need to know more about families’ disposable income changes after
leaving public assistance; about their long-term opportunities for wage and income
growth as their labor market experience grows; and how families whose access to public
assistance has become much more limited cope with the combined demands of work,
parenting, and economic survival. For instance, there is a growing interest in how such
things as chronic child health problems (such as asthma) or parental mental health
(particularly problems of depression) might interact negatively with efforts to become
economically self-sufficient.
Third, there is a need to develop adequate research experience in methodologies
that these new research questions require. This means a better understanding of how to
effectively utilize administrative data sources; a better way to identify and code specific
policy components within welfare reform; a better way to interpret and generalize
program impacts from an increasingly diverse set of state programs; and more credible
ways to identify policy effects and analyze their impacts on long-term behavioral


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Figure 1

Earned Income Tax Credit Subsidy in 2000
2+ child family


Subsidy Amount

slope= .40

slope= -.2106

1 child family
slope= .34
slope= -.1598




Earnings Level



Source for EITC Parameters: “The EITC and the Taxation of Lower-Income Working Families.” Joint Economic Committee Staff Report, March
2000. (http://www.seante.gov/~jec)

Figure 2
Figure 2

Income Constraint Resulting From A Typical Welfare Program



Break-Even Point





Hours of Work
Note: Assumes no income other than welfare benefits and earnings.

G: Maximum Benefit at
0 Earnings
w: Wage Rate
t: Benefit Reduction

Figure 3

Total AFDC/TANF Caseloads





1996 Welfare Reform



Source: Agency for Children and Families, Department of Health and Human Services (http://acf.dhhs.gov)



















Number of AFDC/TANF Households


Figure 4

Labor Force Participation Rates for Women by Marital Status and Children
(Ages 20-65)

Single w/ no kids

Single w/ kids under 18


Married w/ kids under 18


Married w/ no kids

Source: Tabulations of March Current Population Survey Data














Labor Force Participation Rate


Figure 5

Key Demographic Trends, 1970-1999



Marriage Rate



Birth Rate for All Unmarried
Women Ages 15-44




Divorce Rate



Source: National Center for Health Statistics, National Vital Statistics Reports. (http://www.cdc.gov/nchs)


















Birth Rate per 1,000


Marriage and Divorce Rate per 1,000


Table 1

Maximum Benefit Levels Across States
(2000 Dollars)

Selected Points In Benefit




Percent Change

20th Percentile State

$358 (NC)

$319 (IA)

$288 (IN)


Median State

$480 (NE)

$428 (IL)

$379 (DC)


80th Percentile State
$680 (MI) $607 (MD) $546 (WA)
Source: State Policy Documentation Policy (www.spdp.org) and The Urban Institute
Note: Maximum benefit levels for family of three. 51 states (including D.C.) used in

Table 2

Cumulative Cash Welfare Available
During First 24 Months of Work for a
Welfare Recipient with 2 Children


Jan 1996 AFDC Program ($2000)
Hourly Wage = $6/hour
30 hr
40 hr

2000 TANF Program
Hourly Wage = $6/hour
30 hr
40 hr

District of Columbia










New Hampshire





Table 2-continued

New Jersey
New Mexico
New York
North Carolina
North Dakota
Rhode Island

Jan 1996 AFDC Program ($2000)
Hourly Wage = $6/hour
30 hr
40 hr

2000 TANF Program
Hourly Wage = $6/hour
30 hr
40 hr

South Carolina
South Dakota
West Virginia





Median State





Source: Author's calculations from program parameters found in the State Policy
Documentation Project (www.spdp.org) and U.S. House of Representatives (1996).
Note: All numbers in 2000 dollars. Ignores any waivers that affected BRRs in 1995, and
assumes all states are subject to the federally-mandated BRR.

Table 3

U.S. Poverty Rates

Percent Poor
All Families





Families with Single Female Householder





Black Families, Single Female





Hispanic Families, Single Female
Source: The Census Bureau (http://www.census.gov/)
Note: 1979, 1989 and 2000 represent the end of extended periods of economic growth.
1992 is the end of the recession of the early 1990s.

Table 4

Impact of the Safety Net on Poverty Gaps per Person
(All persons in families with children, 1999 dollars)

Poverty Gap
Based on:
Pretransfer Income
Plus Social
Plus Means$1,488
tested Benefitsb
Plus Federal
Percent Reduction in Poverty Gap due to:
Federal Taxes






















a. Includes Social Security, disability, and worker’s compensation.
b. Includes cash benefits, food stamps, housing subsidies and school lunch.
Source: Center on Budget and Policy Priorities (2001).

Table 5

Average Income of Female-Headed Families by Quintile
(1999 Dollars)

Average Disposable Income
Quintile 1
7,714 8,532 8,292
Quintile 2
12,929 14,438 14,403
Quintile 3
16,216 18,971 18,850
Quintile 4
22,568 24,698 25,130
Quintile 5
42,718 47,057 50,801
Source: Tabulations by Center on Budget and Policy Priorities.


% Change

% Change

Table 6

Research on Welfare Reform Impacts
Part A: Econometric Research on Welfare Reform Impacts Using Data Prior to 1996 Welfare Reform



Key Independent

Results on Key Variables

Bartik &

Log(AFDC caseloads
per capita)

Multiple economic
variables (including
unemploymt rates,
Based on state
and local labor market
demand information)
data, 1984-96
Dummy variables
for state waivers
Includes state and year fixed effects. Some estimates include lagged
dependent variable and first difference models.

• Local labor demand information is important in
explaining caseload changes and including these
variables reduces the unemployment coefficient.
• 1% increase in employment growth leads to 4% decline
in caseloads, similar to the effect of a 1% decline in
▪ Gross job flows (high job turnover) is positively
correlated with higher caseloads.


Log(AFDC caseloads
per capita)

• Share of caseload change due to economic factors:
29% in 1990-94
59% in 1994-96
• Share of caseload change due to waivers:
-22% in 1990-94
28% in 1994-96
• 5% estimated change in AFDC caseloads due to
1-point increase in unemployment.

Based on state
data, 1977-96

Multiple economic
variables (including
unemploymt & wage
Dummy variables for
state waivers

Also includes extensive controls for demographic, program and
political variables, along with state and year effects.

Table 6-continued

Council of

Log(AFDC caseloads
per capita)

Unemploymt rates
Dummy variables for
state waivers
Based on state
(looks at overall
waiver effects &
data, 1976-96
policy components)
Also includes state effects, year effects and state time trends.

• Share of caseload change due to economic factors:
24% to 31% in 1989-93
31% to 45% in 1993-96
• Share of caseload change due to waivers:
13% to 31% in 1993-96
• 3% to 5% estimated change in AFDC caseloads due to
1-point increase in unemployment.

Figlio &

log (AFDC caseloads
per capita)

In static models:
• Share of caseload change due to economic effects:
-10% to 36% in 1993-96
• Share of caseload change due to waivers:
0% ro 24% in 1993-96
In dynamic models:
• Share of caseload change due to economic effects:
18% to 76% in 1993-96
• Share of caseload change due to waivers:
-7% to 1% in 1993-96
• 6% to 9% long-run rise in caseloads due to
1-point rise in unemployment rate.

Unemploymt rates
Dummy variables for
state waivers

Based on state
data, 1976-96
Also includes state effects, year effects, and state time trends. Dynamic
models include first-difference and lagged dependent variables.

Levine &

Log(AFDC caseloads
per capita)

Unemploymt rates
Dummy variables for
state waivers

Based on state
data, 1976-96
Also includes state effects, year effects and state time trends.

• Economic effects of same size as CEA (1997) study.
• States with waivers have almost twice the caseload
reduction but no difference in unemployment rates.

Table 6-continued

Log (AFDC participants/
Unemploymt rates
female population,
Dummy variables for
aged 16-54)
state waivers
Weeks and Hours of work
(looks at overall
waiver effects &
policy components)
Based on March CPS data,
aggregated into education &
age cells by state, 1977-95
Also includes state effects, year effects and state time trends, along
with demographic controls.

• Reduction in participation due to waivers:
-1.7 percentage pts among women high school dropouts.
-0.8 to –1.0 percentage points among all women.
▪ Among high school dropouts also find significant effects
of waivers on weeks and hours of work; no significant
effects on earnings or income.
• 0 to 0.3 percentage point rise in participation due to
1-point rise in unemployment rates


• Institutional program operation variables are
highly significant.
• Programs defined as “tough” produce greater
caseload reductions.

AFDC caseload
growth by state
Based on state
data, 1991-96.

Does not include state or year fixed effects.

Multiple economic
variables (including
unemployment rates
and per capita income)
Dummy variable for
“soft” or “tough” state
State program operation
variables (approval rates
exemption rates, work
assignment rates, etc.)

Table 6-continued

Wallace &

Log(AFDC caseloads
per capita)

Multiple economic
variables (including
unemploymt and
Based on state
wage information)
Dummy variables for
data, 1980-96
state waivers
Also includes extensive controls for demographic, program and
political variables, along with state and year effects.

• Share of caseload change due to economic effects:
50% for 1990-94
47% for 1994-96
• Share of caseload change due to waivers:
-13% for 1990-94
22% for 1994-96
• 5% to 6% rise in caseloads due to
1-point rise in unemployment rate.

Davis, &

• No separate estimates of economic effects alone;
66% of change due to economic and seasonal
factors in 1993-96.
• Share of caseload change due to waivers:
-9% in 1993-96.
• 2% estimated change in AFDC caseloads
due to 1-point increase in unemployment
that lasts 5 months.

Log(AFDC caseloads/
Unemploymt rates
Female population,
Dummy variables for
aged 14-55)
individual policy
Based on state
components of
state waivers
data, 1987-96
Also includes state effects, state time trends, time trends (t, t2, t3 ),
and month effects. Estimated models include lagged dependent
variables and first differences.

Table 6-continued

Part B: Econometric research on Welfare Reform Impacts Including Data After the 1996 Welfare Reform



Council of

log(AFDC caseloads
per capita)



Key Independent

Unemploymt rates
Dummy variables
for state waivers and
Based on state
TANF implementn
(looks at overall
data, 1976-98
waiver effects &
policy components)
Includes state effects, year effects, and state time trends.

Results on Key Variables
▪ Share of caseload change due to economic factors:
26% to 36% in 1993-96
8% to 10% in 1996-98
▪ Share of caseload change due to waivers:
12% to 15% in 1993-96
▪ Share of caseload change due to TANF:
35% to 36% in 1996-98

Unemploymt Rates
▪ TANF and waivers have identical (negative) effects
Dummy variables
on participation, creating a 2.1 percentage point decline
for state reforms
(exclusive of time limits).
Based on March
(waivers and TANF)
▪ Time limits have significant negative effects on
CPS data, 1978-98
and for time limits
participation in families with younger children.
Includes state effects and year effects. Also includes demographic controls.
Children’s ages are interacted with time limit dummy variables.
Unemploymt Rates
▪ Time limits have significant negative effects on
(forthcoming) participation
Dummy variables
TANF participation and positive effects on earnings,
Employment measures
for state reforms
especially among women with younger children.
Earnings & income
(waivers and TANF)
▪ No effect of time limits on earnings or income.
Based on March
and for time limits
▪ Significant effect of EITC on welfare use and
CPS data, 1978-99
EITC parameters
Includes state effects and year effects. Also includes demographic controls.
Children’s ages are interacted with time limit dummy variables.

Table 6-continued
Kaushal &


Unemploymt Rates
• States with both time limits and family caps show
Dumy variables
significant increases in employment and hours
for family cap and
among married women with children.
time limits
• Little significant effects of reform on fertility.
Based on March
Also codes reforms
CPS data, 1995-99
by “intensity”
Difference in difference estimates for unmarried women with children,
using married women with children and unmarried women without children
as control groups. Includes state and year effects and demographic controls.
O’Neill &

Employmt last week

Unemploymt rates
Dummy variables
for state waivers and
TANF implementatn

▪ Share of caseload change due to economic factors:
30% in 1992-96; 17% in 1996-99
▪ Share of caseload change due to welfare reforms:
12% in 1992-96 (waiver period)
49% in 1996-99 (TANF period)
▪ Similar effects on employment changes.
▪ Policy effects strongest among younger and
more educated women.

Based on March
CPS data, 1982-99.
Includes state effects, state time trends and national time trend.
No year effects included. Demographic controls included. Separate
groups of single mothers by age, education, and race are analyzed.
Schoeni &
Unemployment or state
▪ Waivers have a significant effect on AFDC participation,
income measures
labor market participation, earnings, income, poverty
Employment measures
Dummy variables
rates, and marital status.
Earnings measures
for state waivers
▪ TANF has significant negative effects on welfare
Income & poverty
and TANF implementatn
participation, larger than the effects of waivers.
Family structure
(Also measures TANF
▪ TANF has relatively small but significant effects
effects as a pre-post
on earnings, poverty rates, and household structure.
Based on March CPS
1996 effect)
▪ Economic factors fully explain labor market changes
data, 1977-99,
in the TANF period.
aggregated into education
& age cells by state
Includes state effects, year effects, state time trends. Also includes demographic controls.

Table 6-continued

Wallace &

log(AFDC caseloads
per capita)

Multiple economic
measures (including
unemployment and wages)
Based on monthly
Dummy variables for
state administrative
state waivers and
data, 1980:1-1998:6
TANF implementatn
Also includes state-month effects. Models estimated in first differences
with lagged dependent variables.

▪ Estimated caseload change due to economic factors:
20% to 36% in 1990-94
8% to 12% in 1994-98
▪ Estimated caseload change due to waivers:
-4% to –5% in 1990-94
26% to 31% in 1994-96
▪ Estimated caseload change due to TANF:
28% to 35% in 1997:1-98:6

Table 6-continued

Part C: Econometric Research on Welfare Reform Impacts Using Flow Data

Stanhope &


Key Independent

Results on Key Variables

Prob(exit welfare
conditional on
spell duration)

Unemployment and
state income
Dummy variables for
individual policy
components in state

▪ Unemploymt not linked to welfare exits.
▪ Work exemptions for mothers with young children
increase welfare exits; earnings disregards decrease
exits; other policy components insignificant.
▪ Primary policy effects on exits from welfare to work.
Non-work-related exits not affected by policy.

Unemployment and
state income
Dummy variables for
individual policy
components in state

▪ Higher unemployment correlated with welfare re-entry.
▪ Work exemptions for mothers with young children make
women less likely to re-enter welfare; other policy
components insignificant.
▪ Some income increases visible over time among welfare

Based on monthly
PSID data on welfare
spells, 1989-96
Uses event history analysis. Also includes demographic controls and state fixed effects
Stanhope &

Prob(Return to AFDC
conditional on time
since leaving AFDC)

Based on monthly
PSID data on postwelfare spells, 1989-96
Uses event history analysis. Also includes demographic controls and state fixed effects.

Table 6-continued

Klerman &

Log (Caseloads
Unemployment rates
▪ Standard estimates based on stock data may be biased.
per capita)
(No policy effects are
▪ Simulated effects of economic factors on caseload
Welfare entry rate
estimable since data
changes between 1995-98 range from 12% to 47%.
Welfare continuation
is from a single state)
Based on monthly
administrative data
from CA, 1989-98
Develop stock-flow model of caseload change. Estimates include county and time fixed effects.

Rokicki &

Welfare exit rate
Welfare entry rate

Unemployment rates
Dummy variables on
significant state
program changes
(including waiver and
TANF implementatn)

Quarterly administrative data from 5
metro areas,
early 1990s-97
Includes site specific dummies, time trends, and quarter effects.

▪ Changes in exit rates explain about 2/3rds of
the caseload decline in 4 of the 5 cities; changes
in entry rates explain 1/3 of the decline.
▪ Economic conditions affect welfare exits, not entries.
▪ State waivers reduce welfare exits by 21%; TANF
reduces welfare exits by 11%.

Table 7

Effects of Financial Incentive Schemes Tested Using Random Assignment
Third Year Effects
I. Programs with Incentives Only
MFIP Incentive Only
Employment (%)
Annual Earnings ($)
Annual Cash Transfers ($)
Annual Income ($)
Poverty (%)

WRP Incentive Only

II. Programs with Incentives and Work Requirements
Full WRP
Employment (%)
Annual Earnings ($)
Annual Cash Transfers ($)
Annual Income ($)
Poverty (%)





CT Jobs First


Iowa FIP




Sources: Employment, Earnings, Cash Transfers, and Annual Income for all programs except NY CAP and Iowa FIP come from
Bloom and Michalopoulos (2001, Appendix Tables C.2 and C.3). Poverty data for MFIP comes from Miller et al (2000, Table 4.5).
Poverty data for SSP comes from Michalopoulos et al (2000, Table ES.2). Data for NY CAP program come from DeMarco and Mills
(2000) and are averages over the first five years after random assignment. Data for Iowa FIP program come from Fraker and Jacobsen
(2000) and are averages over the third year after random assignment. All data in U.S. dollars.
The FTP evaluation provides no information on poverty rates, but reports a 6.0 percentage point positive impact on the question
"usually has enough money at the end of the month" (significant at the 1 percent level).

Table 8
Annual Benefits Received per Dollar Spent in Various Welfare Reform Evaluations

Column 1
Column 2


costs per

Column 4
Column 5


















National Evaluation of Welfare to Work
Strategies (NEWWS, 7 sites)
Maximum (Portland, OR)
Minimum (Riverside HCD, CA)







Greater Avenues for Independence
Program (GAIN, 6 sites in California)
Maximum (Riverside)
Minimum (Los Angeles)







gains per


Self Sufficiency Project (SSP), Canada
Long-term recipients


Minnesota's Family Investment Plan
Single parent urban long-term recipients
Single parent urban recent applicants
Two parent applicants
New Hope Demonstration, Milwaukee, WI

I. Financial Incentives Programs (including
strong work requirements)

II. Mandatory Employment Programs only

* Includes the total imputed value of all program benefits and services to recipients. This includes the income gains represented in
Column 1, as well as the imputed value of health insurance benefits, support services, and fringe benefits.
** It is difficult to calculate comparable cost-benefit ratios for the GAIN Riverside site, since the program increased income to
recipients while generating savings to the government in reduced program costs. In some sense, with government savings the costbenefit ratio is infinite. Of the 6 GAIN sites, 3 increased income to recipients at a cost savings to the government, 2 increased income
to recipients while increasing government costs, and the Los Angeles program reduced income to recipients while increasing
government costs.
Sources and notes:
1. Dollar amounts are calculated over different years for different programs; all in U.S. dollars. See sources for details.
2. SSP: Michalopoulos et al (2000). Column 1 and 2 figures come from table ES-1, page ES-7. Does not include taxes, and
ignores costs of administering program. Effects are over 3 years.
3. MFIP: Miller et al (2000). Column 1 and 2 figures come from tables 4.1, 5.1, and 6.1, and present effects over 10 quarters.
Column 4 and 5 figures come from Table 7.1, and present effects over 5 years. Both sets of numbers include the Earned Income
Tax Credit (EITC).
4. New Hope: Bos et al (1999). Column 1 and 2 figures come from Table 5 of the Executive Summary. Column 4 and 5 figures
come from Table 8.3. Effects are over 2 years.
5. NEWWS: Program benefits come from Freedman et al (2000), Tables 5.1, 6.1, and 6.2. Costs come from Bloom and
Michalopoulos (2001), and are net of savings in transfer payments (AFDC and Food Stamps), which come from Tables 6.1 and
6.2 of Freedman et al (2000). Columns 1 and 2 are not applicable as no additional transfer payments were paid to experimentals.
Does not include the EITC on either the cost or the benefit side. Effects are over 2 years. Riverside ran more than one program.
The results presented above were from the Human Capital Development (HCD) program, which emphasized education first.
6. GAIN: Riccio, Friedlander and Friedman (1994). Columns 1 and 2 are not applicable as no additional transfer payments were
paid to experimentals. Column 4 and 5 figures come from Tables 6b and 7 of Executive Summary. Effects are over 5 years.

Table 9

Research on the Effects of Welfare Reform on Family Structure and Fertility
Part A. Econometric Estimates of Waiver and TANF Effects


Dependent Var

Key Independent Var


Fitzgerald and Ribar

SIPP panels
1990, 1992, 1993

Female headship
*Exits from and
entries to headship

Welfare waivers
• Waivers don’t affect headship
(Aggregate and
by policy component) • Waivers increase exits from and
reduce entries to headship
• Estimated effects of waivers by
policy component often show
wrong sign

Horvath-Rose and Peters

State administrative
panel data

Nonmarital birth

Welfare waivers
• In aggregate, waivers reduce
(aggregate and
nonmarital births
by policy component) • Family caps have negative and
significant effect
• Minor parent provisions have
significant positive effect
• Few effects of time limits,
AFDC-UP or work requiremts

Kaushal and Kaestner

CPS data


Family caps and
time limits

• No significant or credible effects
of family caps or time limits on
childbearing among single
mothers with children.

Table 9-continued
Schoeni and Blank

CPS data,
aggregated to state
level, 1977 – 1999

Among all women:
*Share who
head households
*Share married

Welfare waivers
(aggregate effects)
TANF implementation

• Waivers reduce headship
and increase marriage
• TANF reduces headship

Part B. Econometric Estimates of the Effects of Family Caps


Dependent Var

Key Independent Var


Acs (1996)

Women w/ at least
one child

Probability of
higher order birth

Incremental AFDC

• Negative effect, but insignificant

Argys, Averett and
Rees (2000)


Probability of
pregnancy and

Incremental AFDC

• Positive significant effect on
pregnancy, unless state
fixed effects are included
• No effect on abortion

Fairlee and London

Women w/ at least
one child

Probability of
higher order birth

Incremental AFDC

• Few effects on births

Grogger and Bronars

1980 PUMS

Time to
next birth

Incremental AFDC

• No significant effects

Table 9-continued
Part C. Experimental Evidence on the Effects of Welfare Reform on Family Structure and Fertility

Location and Years

Nature of Intervention


A Better Chance
(ABC) Demonstratn 5 sites
Fein (1999)
Experiment: 1995-96
Final evaluation:
18 months out

Mandatory job search
2-year time limits
Earnings disregards
Strong sanctions
Family caps
Work supports

• Few effects on marriage
• Cohabitation increases among less skilled
and younger mothers
• No fertility effects
• Reduced enthusiasm for childbearing

California Work
Pays Demonstratn
Hu (2000)

4 sites
Experiment: 1992-96
Evaluation includes
data thru 1997

Reduced benefit levels
Increased BRRs

• Significantly more married couples
stay together.
• No significant effects on single
women’s marriage or cohabitation

Family Developmt
Camasso, et. al.
(1998a and 1998b)

New Jersey

Family cap program
• Birth rates 9% lower
Earnings disregards
• Increased family planning use
Work supports
• No change in abortions
Two-parent families
given better access to AFDC

Minnesota Family
Investment Program 7 sites
Miller, et. al. (2000) Experiment: 1994-96
Final evaluation:
3 years out

Work mandates
Large earnings disregard
Service coordination

• Increased marriage among single
long-term recipients
• Reduced separation among married
two-parent recipients

Table 9-continued
New Chance
Quint, Bos, and
Polit (1997)

10 states
16 sites
Experiment: 1989-92
Final evaluation:
3½ years out

Teen Parent
Illinois and NJ
Demonstration Project 3 sites
Kisker, Rangaranjan, Experiment: 1987-91
and Boller
Final evaluation:
6½ years out

Comprehensive services
(education, employment
and life planning) to
AFDC recipients who
were teen mothers and
high school dropouts

• Increased instability in living arrangements
• No effect on pregnancy, births, or

Mandatory participation in • More births in experimental group
employment, education, and (an unexpected effect)
life planning assistance


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