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ESSAYS ON WELFARE, CHILDREN, AND FAMILIES

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ESSAYS ON WELFARE, CHILDREN, AND FAMILIES
By

Yi Zhu

A DISSERTATION

Submitted to
Michigan State University
in partial fulfillment of the requirements
for the degree of

DOCTOR OF PHILOSOPHY
Economics

2009

ABSTRACT

ESSAYS ON WELFARE, CHILDREN, AND FAMILIES
By
Yi Zhu

This dissertation examines the economic impacts of social and welfare policies on
children and their families in both developed and developing countries, with particular
focus on the low-income or disadvantaged population.

Chapter 1 looks at the US. foster care system. This chapter first uses recent data
to reexamine the effects of payments to non-kin parents on the total quantity and specific
types of foster care services. In contrast with Doyle and Peters (2007) and Duncan and
Argys (2007), so far the only two relevant studies relying on national samples, the
chapter finds weaker effects of foster care payments. Next, the chapter goes beyond
previous research by exploiting state-specific kinship policies to construct explicit
measures of economic incentives for kinship caregivers, that is, the licensing flexibility
and monthly subsidies offered to kin. Linking national micro-level data of foster children
to state policies, the chapter then estimates the effects of economic incentives for kinship
and non-kin families respectively on the placement arrangements of children entering
foster care. The results suggest that reducing licensing costs by relaxing the standards
increases the use of kinship care, but increasing subsidies has little effect on the
placement. Further analysis provides some evidence that state policy changes can be
endogenous.

Chapter 2 tests the effect of fertility on marriage stability using instrumental

variables that are based on a unique birth control policy in China to break simultaneity.

The one-child policy, an affirmative birth control policy that applies to the Han but not to
the ethnic minorities, constitutes a natural experiment. It enables us to identify the effect
of fertility on marriage stability by introducing exogenous variation in fertility that has
resulted from the enactment of the one-child policy. Employing the Chinese Population
Census data, we find that the policy has a strong effect on reducing second births. We
also find that having a second child is negatively associated with the probability of being
divorced, but there is little evidence of a causal effect when we identify fertility by the
exogenous birth control policy.

Chapter 3 focuses on the US. child care assistance programs that have been
designed to help low-income families pay for the care and education of their children
while parents work and/or participate in education and training. The 1996 welfare reform
restructured the US. child care assistance programs by creating a single block grant, the
Child Care and Development Fund (CCDF). Given that the CCDF gives states substantial
flexibility in setting program rules such as family co-payment levels and reimbursement
rates, this paper combines data from the Current Population Survey and state policy
surveys from 2001 to 2007 to examine the effects of child care subsidies on subsidy
receipt and employment of single mothers in a postreforrn period. The results suggest a
weak effect of child care subsidies on the likelihood of receiving subsidies or being

employed, though subsidies are found to have a small effect on increasing full-time work.

To my parents, Lili Wang and Yude Zhu.

iv

ACKNOWLEDGEMENTS

This dissertation has benefited greatly from guidance, cements, and support
from Steven Haider, my advisor. His insightful and challenging questions through the
many drafts of this dissertation have made it a much better product than it would have
been. His keen perception and understanding of economic issues have greatly sharpened
my focus. All of my future development as an economist will be built upon what he has
taught, or attempted to teach, me.

I would also like to thank Todd Elder, Gary Solon, and Stephen Woodbury for
their invaluable guidence and insights at various stages of the process. Further, I would
like to thank my coauthors, Hongbin Li and Junsen Zhang, for their significant contri-
bution to the second chapter.

In addition, many people deserve my thanks for having offered help on various
parts of this dissertation. In particular, I am gratefiil for extensive comments and
suggestions from Soren Anderson, Jeff Biddle, and participants at the 2008 UM-MSU-
UWO Labor Day Conference and seminars at Michigan State University. I thank Ama
Agyemang, Mary Chaliman, Angelique Day, Helene Ellis, and Joseph Kozakiewicz for
discussions on child welfare issues, and to staffs of various State Departments of Health
and Human Services for providing information on kinship policies. I also acknowledge
the National Data Archive on Child Abuse and Neglect at Cornell University for kindly
providing the data from the Adoption and Foster Care Analysis and Reporting System.

Friends, fellow graduate students and department personnel have offered immense

support, both intellectually and emotionally. In particular, I would like to thank Meng-

Chi, .Wei-Chih, Jingiing, Lenisa, Na, Ren, Nanyun, Simon, Wei-Siang, Shengwu,
Jennifer, Margaret, and the rest for their years of help.

Finally I am greatly indebted to my parents, who have enthusiastically supported
and encouraged me throughout my years of education. I am beyond words to express my

gratitude and the least I can do is dedicate this dissertation to them.

vi

TABLE OF CONTENTS

List of Tables ..................................................................................... ix
List of Figures .................................................................................... xi
Chapter 1

Do Higher Subsidies Attract More Foster Families? The Effects of Economic

Incentives on Foster Care Placement .......................................................... 1

1. Introduction .............................................................................. 2

2. Background: Placement, Licensing, and Payment .................................. 6

2.1 Placement Decision Making ................................................. 6

2.2 Licensing and Payment ...................................................... 8

3. Data ....................................................................................... 9

3.1 Policy Data ...................................................................... 9

3.2 Foster Child Data ............................................................. l4

4. Reexamining Previous Work .......................................................... 16

5. Estimation ................................................................................ 20

5.1 Empirical Model .............................................................. 20

5.2 Effects of Economic Incentives ............................................. 21

5.3 Leads and Lags of Economic Incentives .................................. 24

6. Conclusrons 25

Appendix ..................................................................................... 34

References .................................................................................... 41
Chapter 2

One-Child Policy, Fertility, and Divorce ...................................................... 44

1. Introduction .............................................................................. 45

2. The Birth Control Policy and Marriage Stability in China ......................... 50

2.1 The One-Child Policy ......................................................... 50

2.2 Marriage and Divorce ......................................................... 53

3. Empirical Model ........................................................................ 54

4. Data ........................................................................................ 57

5. The Effect of the One-Child Policy on Fertility ..................................... 59

5.1 The Pre-Treatment Group .................................................... 60

5.2 The DD Estimation ............................................................ 62

5.3 Sensitivity Tests ................................................................ 65

6. The Effect of Fertility on Divorce 7O
7. Conclusrons 72

Appendix ..................................................................................... 84
References .................................................................................... 90
Chapter 3
Child Care Subsidies and Employment of Single Mothers .................................. 94

vii

1. Introduction .............................................................................. 95

2. Child Care Assistance Programs ....................................................... 98
3. Data ..................................................................................... 100
3.1 Child Care Subsidies ........................................................ 100

3.2 Other Data ..................................................................... 103

4. Estimation .............................................................................. 106
4.1 Work Incentives in Child Care Subsidies ................................ 106

4.2 Effects of Child Care Subsidies ............................................ 108

I 5. Conclusrons 110
Appendix ................................................................................... 119
References .................................................................................. 1 22

viii

LIST OF TABLES

Table 1.1 Descriptive Statistics: AFCARS Sample ..................................................... 29
Table 1.2 OLS Estimates of the Effects of Foster Care Payment: State-Level Data... 30

Table 1.3 Marginal Effect Estimates of the Effects of Foster Care Payment:

AF CARS ............................................................................. 31
Table 1.4 Estimates of the Effects of Economic Incentives: AFCARS .................. 32
Table 1.5 Estimates of the Leads and Lags Effects of Economic Incentives:

AF CARS ............................................................................. 33
Table 1.6 Data Sources ......................................................................... 38
Table 1.7 Definitions of State Kinship Licensing and Payment Policies ................ 39
Table 1.8 Summary of State Kinship Licensing and Policies ............................. 40

Table 2.1 Descriptive Statistics for the 1990 Census: Ever-Married Women Aged
20-64 .................................................................................. 78

Table 2.2 Differences-in-Differences Estimates of the Effect of the One-Child
Policy on the Probability of Having a Second Child: 1990 Census .......... 79

Table 2.3 Differences-in-Differences Estimates of the Effect of One-Child Policy
on Other Fertility and Education Outcomes: 1990 Census .................... 80

Table 2.4 Differences-in-Differences Estimates of the Effect of One-Child Policy
on Migration and Labor Market Outcomes: 1990 Census ..................... 81

Table 2.5 OLS and ZSLS Estimates of the Effect of Having a Second Child on

Divorce: 1990 Census .............................................................. 82
Table 2.6 OLS and ZSLS Estimates of the Effect of Having a Second Child on

Divorce: 1990 Census (Rural vs. Urban) ......................................... 83
Table 2.7 Descriptive Statistics: 1982 and 1990 Censuses ................................ 89
Table 3.1 Summary Statistics on Child Care Subsidies by Year ....................... 114
Table 3.2 Child Care Subsidy and CCDF Expenditure .................................. 115
Table 3.3 Descriptive Statistics on Single Mothers with Children under 13.......... 116

ix

 

V!“- -

Table 3.4

Table 3.5

Table 3.6

Table 3.7

OLS Estimates of the Effects of Child Care Subsidies and Other

Policies ............................................................................. 117
OLS Estimates of the Effects of Child Care Subsidy by Child Age ....... 118
Federal Poverty Level and Minimum Wage Earnings ....................... 120

OLS Estimates of the Effects of Child Care Subsidy (without Other
Welfare Policies) .................................................................. 121

Figure 1.1
Figure 1.2
Figure 1.3

Figure 2.1

Figure 2.2

Figure 2.3

Figure 2.4

Figure 2.5

Figure 2.6

Figure 2.7

Figure 2.8
Figure 2.9

Figure 3.1

LIST OF FIGURES

Number and Rate of Foster Children: 1985-2007 ............................. 27
Changes in Kinship Foster Care Entries and Payments ....................... 28
Foster Care Payments and Kinship Payments .................................. 37
Probability of Having a Second Child by Cohorts: Whole Sample for

1982 and 1990 Censuses ........................................................... 74
Probability of Having a Second Child by Cohorts: Han Sample for

1982 and 1990 Censuses ........................................................... 75
Probability of Having a Second Child by Cohorts: Minority Sample for

1982 and 1990 Censuses ........................................................... 75
Probability of Having a Second Child by Cohorts: Han-Minority

Differences for 1982 and 1990 Censuses ........................................ 76
Probability of Being Married by Cohorts: Han-Minority Differences for

1982 and 1990 Censuses ........................................................... 76
Probability of Having a First Child by Cohorts: Han-Minority

Differences for 1982 and 1990 Censuses ........................................ 77
Probability of Other Outcomes by Cohorts: Han-Minority Differences

for 1982 and 1990 Censuses ...................................................... 77
Probability of Having a Second Child by Year (1982 Census).... . . 87
Probability of Having a Second Child by Year (1990 Census)............... 88
Distribution of Child Care Subsidy ........................................... 119

xi

Chapter 1
Do Higher Subsidies Attract More Foster Families? The Effects

of Economic Incentives on Foster Care Placement

1 Introduction

The foster care system in the U.S., which provides substitute care for children who are
temporarily removed from their parents due to abuse or neglect, has grown dramatically in
the past two decades. Figure 1.1, which presents the statistics released by the Department
of Health and Human Services (DHHS), shows that 514,000 children were using foster
care in 2005, almost doubling in number since 1985. The proportion of children in foster
care has increased likewise from 4.3 to 7.0 per 1,000 children during this period. The
fast growth in foster care caseloads during the 19805 and 19908 has been widely believed
to be associated with parental substance abuse, crack cocaine and HIV/ AIDS epidemics,
parental incarceration, and poverty and cash welfare (Swann and Sylvester, 2006; Doyle
and Peters, 2007). Both the number and proportion of foster children peaked in 1999 and
have been slowly decreasing Since then.

Foster care aims to ensure the health and safety of children in custody who would oth-
erwise live in an abusive family environment. Foster homes are supervised and supported
by state child welfare agencies. On average, foster parents are paid a subsidy of $480 (in
2005 dollars, calculated by the author) per month per child. Each year states spend more
than $20 billion on foster care and other child protective services (Center for Law and
Social Policy and Children’s Defense Fund, 2006).

The late 19808 and 19903 have also witnessed a. fast growth in the use of relatives to care
for foster children, probably due to combined effects of increasing demand for foster care,
declining supply of non-kin parents, and a more positive attitude of child welfare agencies

toward the use of kin (US DHHS, 2000; Geen, 2004).1 Although early national data are

 

1Besides kinship foster care, the private kinship care outside the child welfare system (children
not in state custody) has also become more prevalent. Although it is also important, the private

scarce, available evidence suggests that the proportion of kinship placement. among all
foster children increased from 18% in 1986 to 31% in 1990 (Kusserow, 1992), with a large
contribution from California, Illinois, and New York (Harden et a1., 1997). The share of
kinship foster care has leveled off in recent years, and now roughly one-quarter of foster
children are placed in related family homes and one-half in unrelated homes (US DHHS,
2006). Moreover, a further look at foster care placement reveals a substantial amount of
variation in the use of kinship homes across states. For example, in 2005, kinship care
accounted for more than 40% of foster care cases in Florida and Illinois, whereas merely
5% of foster children in Virginia were placed with kin.

The increasing reliance on kin as foster parents has made kinship care an important
policy and practice issue, as children and caregivers in kinship homes are found to differ
in significant ways from those in non-kin homes.2 Although now almost all states give
preference to kin when a child is determined to be removed from home (Jantz et al., 2002),
debate continues on how kinship foster parents should be financially assisted and how
they should be assessed differently from regular foster parents in terms of meeting the
child welfare goals of safety, permanency, and well-being (Shlonsky and Berrick, 2001). As

a result, states differ greatly from each other in how they license and subsidize kinship

 

kinship care is not very relevant to this study because it is institutionally different from foster care.
Usually the private care is voluntarily arranged by the child’s family without the intervention of
child welfare agencies, but most of the foster care (over 90 percent of the cases) is court ordered
following the reported abuse or neglect. Hence in general it is unlikely for families to freely switch
between the private and foster kinship care. Unless otherwise specified, “kinship care” generally
refers to kinship foster care in the following analysis.

2In general, researchers have well documented the differences in demographic and socioeco-
nomic characteristics between kinship and non-kin foster care, but it still remains inconclusive
whether kinship care is more beneficial for children in terms of permanency and well-being out-
comes. Not only is the research on developmental outcomes much less extensive, but one also
needs to be cautious when interpreting these outcome findings as the comparisons can be plagued
by the selection bias that children in kinship and non-kin care might be systematically different
even prior to the removal. For detailed reviews, see Kang (2003a, b), Cuddeback (2004), Geen
(2004), and numerous studies cited therein.

 

V‘s-2.1» , - _. -

caregivers. The goal of this paper is to explore to what extent the differences in licensing
and payments are related to the variation in foster care placement. (i.e., kinship, non-kin, or
group homes). Would raising subsidies be an effective way to attract more kin to provide
foster care? Better understanding of such questions will have significant policy implications
on how to improve the use of a desired type of care.

Given the large body of literature on comparisons of kinship versus non-kin placement,
surprisingly little is known about the effects of economic incentives on the placement.
Only two recent studies have linked foster care payments to the quantity of foster care
provided using national samples.3 Doyle and Peters (2007) use a panel of state-level data
from 1987 to 1995 to estimate the relationship between the rate of children in foster care
and the monthly subsidy. Their estimates of a quadratic specification suggest a positive
relationship for states with low subsidy rates below a certain point. Meanwhile, Duncan
and Argys (2007) look at how foster care subsidies affect the specific types of placement,
using a micro-level sample of children entering foster care from the 1998 Adoption and
Foster Care Analysis and Reporting System (AFCARS). They find that higher foster care
payments significantly increase the probability of placement in non-kin homes and reduce
the likelihood of placement in kinship or group homes.

Nonetheless, both studies share a common problem that they use only the foster care

subsidy to capture the effects of economic incentives but fail to take into account that in

 

3Several early studies, usually based on small scale surveys or experiments in selected states,
suggest that higher subsidies increase the total quantity of foster care services (Simon, 1975;
Campbell and Downs, 1987; Chamberlain et al., 1992; Testa and Rolock, 1999). More recently,
Doyle (2007) tests the effect of a 1995 policy change in Illinois that lowered the subsidy paid to
relatives on the supply of kinship foster care. The results indicate that kin offered the 27% lower
subsidy after the reform were 10-15% less likely to provide care. Another strand of literature
uses state-level panel data to examine the effects of state-specific characteristics on child welfare
caseloads, but these studies typically stress demand-side factors and rarely include foster care
subsidies (see, e.g., Paxson and Waldfogel, 2002, 2003; Swann and Sylvester, 2006).

many states kin are licensed and subsidized differently from non-kin caregivers.4 While
foster care subsidy can be used to measure the payment to non-kin foster parents, only
part of the kinship parents are paid foster care subsidies. Hence the estimate of this
single parameter would be difficult to interpret because it could pick up a mixed effect of
incentives for different types of caregivers.

Using multiple years of more recent AFCARS data, this paper first reexamines the
effects of foster care payments on the total quantity and specific types of foster care services.
In contrast with Doyle and Peters (2007) and Duncan and Argys (2007), the findings
suggest weaker (in both economic and statistical significance) effects of foster care subsidies,
possibly due to the difference in sampling periods (for Doyle and Peters) and a better
control for unobservable state characteristics thanks to more years of data (for Duncan
and Argys, who use a single-year cross—sectional sample).

Next, the paper goes beyond previous research by exploring more deeply the state-
specific policies concerning licensing and subsidizing kinship caregivers. Such information
makes it feasible to construct explicit measures of economic incentives for kinship care-
givers, that is, the licensing fiexibility and monthly subsidies offered to eligible kin for each
state. In this way, it is then possible to test the effects of economic incentives faced by
different types of foster parents on the use of a specific type of care. Combining policy
data for 1997, 1999, 2001, and 2005 with the AFCARS data of children entering foster
care, the study finds that relaxing licensing standards for kin (thus reducing their costs to

obtain licenses) is associated with more use of kinship care and less use of non-kin care,

 

4Although both studies try to control for the effects of kinship policies by including a variable
indexing the stringency of state licensing of kinship care, the classification they borrow from Boots
and Geen (1999) is confusing and needs to be recoded (see note 14). More importantly, given
that this type of policy is likely to change over time, applying Boots and Geen’s single-year policy
to all years is inappropriate (and it also has to be dropped in state-effects analysis). Regardless,
this variable turns out not to be statistically significant in either study.

 

\ .a..

but there appear to be little effect of either kinship payments or foster care payments on
the placement. However, further analysis of the leads of state policy variables implies that
some policy changes may be endogenous, suggesting caution in the interpretation of the
main findings.

The remainder of the paper is organized as follows. Section 2 provides background of
the practice in foster care placement, as well as state policies of licensing and subsidizing
foster parents. Section 3 describes the data. Section 4 updates two previous studies (Doyle
and Peters, 2007; Duncan and Argys, 2007). Section 5 presents the empirical model and

estimation results. Section 6 concludes.

2 Background: Placement, Licensing, and Payment

2.1 Placement Decision-Making

When a child is removed from his or her home due to abuse or neglect,5 state child welfare
agencies are required to establish a foster-care case plan that. is in the best interest of the
child.6 An important part of the case plan is to achieve the most appropriate out-of—home
placement that serves the permanency goal and special needs of the child. Kinship family
homes, non-kin family homes, group homes. and institutions are the major types of foster
care arrangement.7 Family homes maintain children in a family setting where they live
with foster parents who have been trained, assessed, and licensed to provide shelter and
care. Group homes or institutional care (also known as residential care) are more restrictive

settings that usually accommodate children with special physical or behavioral needs that.

 

5Sometimes children may also enter foster care due to the absence of their parents resulting
from illness, disability, or death, or to their own behavioral problems or disability.

6More institutional background of how children enter foster care is described in the Appendix.

7Other placement types, which are rarely seen and thus not considered here, include pre-
adoptive home, supervised independent living, runaway. and trial borne visit.

cannot be met in regular family homes.8

To determine which kind of placement should work best for the child. a social service
caseworker must take into consideration many factors. In practice, placement decisions are
based on an evaluation of a full set of criteria including the goal of permanence for the
child, the child’s safety, physical, and emotional needs, the racial and ethnic background of
the child, the possibility of placement with siblings, proximity to the child’s original family,
and the availability and capacity of potential settings that can meet the child’s needs.

Although the federal legislations do not specify standardized assessments to make place-
ment decisions, they have provided guidelines and required states to establish standards
and procedures consistent with the law. The Adoption Assistance and Child Welfare Act
of 1980 and the Adoption and Safe Families Act (ASFA) of 1997 both mandated that a
child removed from home be placed in the least restrictive, most family-like setting avail-
able that is located in close moximity to the parents’ home and in the best interests and
needs of the child (Doran and Berliner, 2001).

This federal requirement suggests a hierarchy in the placement decision. In general,
child welfare agencies rank kinship homes. non-kin families, and group homes (or insti-
tutions) as placement settings from least. to most restrictive (Doran and Berliner, 2001).
Thus many states have interpreted the federal principle as an unstated preference for the
use of kin as foster parents (Malm and Bess, 2003), and in practice, policies in almost all
states require caseworkers to seek out kin first (Jantz et al., 2002).

Also in keeping with the federal guideline, children would be placed in a family rather

than in a group home whenever possible.9 It is always expected that placement in a group

 

8These settings include community-based group homes, campus-style residential facilities, and
secure facilities.
9One of the DHHS‘ child welfare outcome goals is to “reduce placements of young children in

it

setting should be the alternative of last. resort. However, in some cases, children with
special needs unmet by family homes may only be suitable for a more restrictive setting.
For example, some may have extensive physical or behavioral difficulties and/ or serious
emotional disturbance. Some adolescents who are at a developmental stage of moving away

from family toward independence may not be ready to form bonds with a new family.

2.2 Licensing and Payment

To ensure children’s safety during their stay in foster care, states use licensure as a pri-
mary method to assess whether foster parents are qualified and able to care for children.
Although varying by states, a typical licensing process would involve a home study, par-
enting training. a criminal background check, references, health statements, minimum age
and income requirements, etc. Licensed caregivers are provided supervision and support
services by state child welfare agencies. They also receive a monthly payment for each
child in care, which is subsidized by federal, state, and local dollars. If the child is eligible
for federal reimbursement under Title IV—E of the Social Security Act,10 much of the costs
would be shared by federal funding. Regardless of who pays the bill, states are free to set
their own rates of foster care payment.

While states require licensure for any non—kin provider, they are given limited guidance
regarding how to approach kinship foster care because the system was not initially designed
to meet the needs of kinship caregivers. Most kinship foster parents were financially assisted

by the Aid to Families with Dependent Children (AFDC) program until, in 1979, the US.

 

group homes or institutions.” This reflects the current emphasis on deinstitutionalization: “The
Department believes that such placements [group homes] should only be considered after other
less restrictive and/ or more family-like options have been seriously pursued” (US DHHS, 1998).

10The major elements of Title IV-E eligibility require that the child has been removed from
his or her home via a voluntary agreement or a court order, the child is in state custody, and
the child’s birth family met welfare eligibility when the child was removed. See US DHHS (2000
p.18) for full details.

Supreme Court ruled that states must make the same foster care payments to kin caring
for Title IV—E-eligible children as they make to non-kin caregivers, as long as kin meet the
same licensing standards. The ASFA of 1997 and the ASFA Final Rule of 2000 further
made it clear that states can be reimbursed by federal dollars for kin caring for Title IV-E-
eligible children only when kin meet the same licensing standards as non-kin family homes.
In addition, waivers for certain non-safety standards can only be granted on a case-by-case
basis.

Although the federal government. would not reimburse states for subsidies paid to kin
who are not licensed the same as non-kin parents, the ASFA did not prohibit states from
assessing kin differently than non-kin or financially supporting these kin using state or local
funds. States were left with latitude in whether or not providing different assessment and
payment options to kin who are unable to meet all of the non-kin licensing requirements.11
Therefore, there has been a significant variation across states in their approaches to li-
censing and subsidizing kinship foster care, and these policies have also evolved over time
within states. This will be shown in the following section, which describes the policy data

in details.

3 Data

3.1 Policy Data

The policy data used in the paper are. built on three surveys of state kinship care policies
by the Urban Institute in 1997, 1999, and 2001 (Boots and Geen, 1999; Leos-Urbel et al.,

2000; Jantz et al., 2002), and the 2005 state fact sheets for grandparents and other relatives

 

“T his flexibility may reflect a tradeoff between the benefits of maintaining family continuity
by living with related ones and the concern that loosed licensing standards may threaten child
safety (Jantz et al., 2002).

raising children (AARP Foundation et al., 2005)."2 Particular attention is paid to whether
states allow kin to be licensed based on different standards than non-kin foster parents, and
if so, the payment option offered to kin. Note that these surveys do not collect information
on the timing of policy implementaticm, so they can only provide a point-in—time snapshot.
of state policies for those four years and the possibility is not ruled out that policy changes
may happen during unobserved years between.

The definitions of measures of state kinship policies are given in Table 1.7 in the Ap-
pendix. In terms of licensing practices. states can be classified into three mutually exclusive
categories: kinship foster parents 1) must meet the same licensing standards as non—kin
caregivers (fall licensure); 2) are assessed based on the same standards as non-kin but some
requirements unrelated to safety could be waived (waived licensure); and 3) are assessed
based on kin-specific standards that. are separate from non-kin (separate approval).13 This
set of licensing indicators is used as a proxy for the difficulty (or costs) of kinship caregivers
in acquiring licensure or approval relative to non—kin providers in each state.

Although usually kin-specific standards are also less stringent than non-kin standards,
separate approval is distinguished from waived licensure because they may imply different

levels of barriers removed in favor of approving kin of giving care.14 The most commonly

 

1“‘*See Table 1.6 in the Appendix for data sources and website links.

13Technically, almost all states having alternative options still allow kin to be licensed the same
as non—kin homes. Although there exist no complete state data on how many kin choose to be
assessed by non-kin requirements, anecdotal evidence from some states (including author’s com-
munications with some state child welfare staffs) suggests a rather low rate of “full licensure"
among relative caregivers. Doyle (2007) points out that in Illinois, each year about 5% of relative
caregivers became licensed at the beginning of the care, and the rate increased to just 12% in
the first year. Jantz et al. (2002) estimate that on average, more than 80 percent of kin were
assessed by waived or separate standards in states that offered these options and also reported
the statistics. One possible reason for the low take-up rates is that many existing foster parent
regulations are designed based on “middle-class values” of what a home should look like (Tem-
pleman, 2003), and many families taking in related children do not have the resources to meet all
those regulations, even given the incentive of potentially higher subsidies when becoming licensed
(Ingram, 1996).

1“Boots and Geen (1999) compress both waived licensure and separate approval into a single

10

waived standards are space and parent training requirements. Some states may also waive
age, income, or other requirements as long as they do not jeopardize child safety. But
in general, separate standards could go further than just waiving space or training re-
quirements. In some cases states only require a minimum level of home study and simple
background check (e.g., a state-database check rather than a fingerprint FBI check) to
approve a kinship home. Kin assessed by separate standards are sometimes referred to
as “approved,” “unlicensed,” or “uncertified” by various states, which in part reflects a
significant difference in treating those kinship caregivers.

The payments that kin are eligible to receive are closely linked to how they are licensed
or approved.15 All full-licensure states make state— or federally funded foster care pay-
ments to kin. Among waived-licensure states, many still provide foster care payments to
kin, but a few of them offer only Temporary Assistance for Needy Families (TANF) child-
only grants,16 or make foster care payments if the child is Title IV -E eligible and TANF
otherwise. Finally, with a few exceptions, separate-approval states do not pay foster care
subsides to kin; they either offer TANF payments or provide some “standard of need” pay-
ments that fall between TAN F and foster care payments. Note that a particular licensure

alternative does not entirely determine which kind of payment the correspondingly-assessed

 

indicator that the state imposed less stringent licensing standards on kin, and interact this in—
dicator with payment options to categorize states. This results in a mix of states with different
licensing options in the same category. As they do not specify which state was of waived licensure
or separate approval, the 1997 licensing policy is recoded based on reported changes in polices
between 1997 and 1999 (Leos-Urbel et al., 2000 Table 5).

15Other than monthly subsidies like foster care and welfare payments discussed here, some
additional benefits (typically paid on a semi-annual or annual basis), such as clothing and holiday
allowances, may also differ conditional on the licensure status. However, most of such benefits
are comparably small, and state data on how they are associated with licensing options are
unavailable.

16Regardless of the custody status of children, all kinship caregivers who are related by blood,
marriage, or adoption are eligible for a TANF child—only payment, which is usually much lower
than a foster care payment.

11

kin can receive. In other words, states in the same licensing category may still choose dif-
ferent payment options. While foster care payments measure the subsidy paid to non-kin
caregivers, these state-specific payment policies make it possible to construct a measure of
the subsidy paid to kin for each state.

The data on the basic monthly foster care maintenance rates are provided by Boots
and Geen (1999) and the Child Welfare League of America National Data Analysis System
( N DAS). The analysis uses the average rates of state foster care payments for children aged
2, 9, and 16, and all subsidy rates (as well as the TAN F rates below) are converted to 2005
dollars. One limitation is that the payment data were collected every the other year and
do not exactly match with the years of policy data. As a result, except for 1999, the foster
care rates for the previous year are used. This appears not to be a big concern as states
adjust their rates slowly over time.17 In addition, a few states need to be dropped because
of missing data on payments.

The annual data on AFDC /TAN F benefits for 2-person families are created by the
University of Kentucky Center for Poverty Research. Without direct data on child-only
payments for policy-data years, the 1995 data (from Geen and Waters, 1997) are used to
calculate the ratios of child-only benefits to 2-person—family benefits for each state. Then
the child-only benefits for other years are imputed by multiplying the 2—person-family
benefits for each year by the 1995 ratios, assuming that each state should adjust welfare
benefits in different categories by roughly the same state-specific rate over time.

In sum, a complete state policy profile used in the analysis includes a vector of licensing

 

17After all converted to 2005 dollars, the average change in foster care payments over a two-year
span in the NDAS data is below 5 percent. On the other hand, this may cause problems because
the following fixed effects analysis requires large variations in payments over time. But given the
currently available data, this is the best measure to use.

12

indicators (full licensure, waived licensure, and separate approval), foster care payment
(subsidy paid to non-kin parents), and kin payment (subsidy paid to kin).18

Table 1.8 in the Appendix presents the distribution of state policies for 1997, 1999, 2001,
and 2005, respectively. Several aspects are worth noting. First, clearly there is variation
in licensing and payment policies across both states and years. Between 1997 and 1999,
14 states changed licensing or payment options or both, 19 states did so between 1999 and
2001, and 19 between 2001 and 2005. Second, overall, states had changed toward more
stringent licensing within these years (although some have moved reversely). This is not
surprising because the ASFA of 1997 and its Final Rule of 2000 may to a large extent have
reduced states’ incentives to support kin who are unable to meet non-kin requirements,
in which cases states can no longer claim federal reimbursement and have to rely on their
own funds. Finally, as expected, states with more flexible licensing options were more
likely to pay less generously to kin (in comparison to foster care payments to non-kin).
The majority of states having a separate approval process chose to offer TANF rather than
foster care benefits.

The variation in amounts (in both levels and changes) of foster care and kin payments
is shown in Figure 1.3 in the Appendix. The foster care payment ranges between $280
(Missouri) and $880 (District of Columbia), with an average of $479 (s.d. = $107). The
kin payment. has a mean of $368 (s.d. = $163), with a minimum of $70 (Mississippi) and

a maximum of $880 (District of Columbia). The figure also indicates that foster care

 

l‘3Another state variable, which is also controlled for in the analysis, measures the broadness of
how states define kin. While some states restrict kin to be only those who are related by blood,
marriage, or adoption, some other states treat anyone who has strong emotional bond to the child
as kin, such as neighbors or close family friends. Since this measure may pick up more of the
state efforts in seeking out kin than the incentives for kin to give care, its discussion is omitted.
The coefficient on this variable is not. statistically significant and excluding it does not affect the
results.

13

payments are generally higher than (if not the same as) kin payments, and kin payments

tend to change more dramatically over time than foster care payments.

3.2 Foster Child Data

The micro-level data on foster children come from the AF CARS, a federal annual data
collection that provides case-level records for all children served by the foster care system
from October 1 to September 30 of the following year. Submitted by states since 1995,
the AFCARS records approximately 800,000 cases each year.19 The main variables in-
clude a child’s demographic characteristics, case details on removal, placement, case goal,
exit (if happening during the current year), and limited information on former and foster
caregivers.

To match with the years for which state policies are available, the AFCARS data of
1997 (version 1), 1999 (version 4). 2001 (version 3), and 2005 (version 1) are used to carry
out the analysis. To be included in the sample, the child must be placed with a kinship
home, a non-kin home, a group home. or an institution.20 Also, to better match foster care
placements with current state profiles, the sample is restricted to children aged below 18
who entered the foster care system during the current year. Nevada is dropped because
the state did not identify the placement. settings for the majority of children in the data.

Finally, merging the AF CARS sample with the state policy data leaves a sample of 826,775

 

1”A child can have multiple records if he or she leaves and then reenters foster care during the
same year. Moreover, it was not until 1998 that penalties established by AF CARS regulation
became applicable. Thus samples prior to 1999 were often partial and incomplete as some states
did not submit their data. The 1997 data include about 400,000 observations, and the 1998 data
contain about 700,000 observations.

20The AFCARS data define “group home” as a licensed or approved home providing 24-hour
care for children in a small group setting that generally has from 7 to 12 children, and “institution”
as a child care facility operated by a public or private agency that provides 24—hour care or
treatment for children who require separation from their own homes. Because group homes and
institutions have similar features that make them distinct from a family-based setting, in the
analysis they are treated as the same type (group home).

14

children from 18, 48, 49, and 46 states in 1997, 1999, 2001, and 2005, respectively.

Table 1.1 reports the main characteristics of the full sample and of three subsamples by
the dependent variable, a child’s most recently reported placement setting. Overall, kinship
and non—kin families account for 26% and 50% of the total placements, and the remaining
24% are placed in group homes. Half of the children live in states where kin are assessed
separately from non-kin parents, and 30 percent stay in states where kin must meet the
same requirements. The child-level explanatory variables include gender, age when last
placed, race, disability status, whether parents’ rights are terminated (not shown), reasons
for removal, and age and marital status of the principal former caretaker prior to removal.

Comparisons of policy variables across placement types first reveal that over 60 percent
of children placed with kin are living in separate-approval states, which is higher than the
proportion for children in non—kin or group homes. Such a correlation between separate
approval and kinship care is also pronounced when the sample is broken by licensing options
(not shown). More than 30 percent of foster children in separate-approval states are cared
for by kin, compared to only 20 percent in either full- or waived-licensure states. This
pattern is in line with the perception that the separate assessment could be much more
flexible than other options and thus greatly reduce the costs for kin to get approved. In
contrast, the relationship between placements and payment measures are not as clear, with
both foster care and kin payments being slightly lower for children in kinship care.

Table 1.1 also indicates that several child characteristics significantly differ among place-
ment settings. For example, consistent with previous research, children living in kinship
homes appear to be younger, more likely to be black, less likely to be disabled, and more
likely to have been removed due to abuse or neglect. There seems to be a sharper contrast
between family homes and group homes in terms of child ages and behavioral problems.

15

An average child placed in group homes is 13 years old, almost twice as old as an aver-
age child in kinship or non-kin care. Nearly 50 percent of the children living in group
homes have been removed due to their own physical or behavioral problems, much larger
than the corresponding proportion in family care (6.1% for kin and 13% for non-kin). Not
surprisingly, these features reflect the practice that group homes and institutions more
often admit children with extensive physical or behavioral difficulties that cannot be met
in family settings. They are also more likely to accommodate older children who are at a
developmental stage when they are not ready to form bonds with a new family.

Next the sample is aggregated at the state level to graphically detect any potential
interactions between state variables. Figure 1.2 shows the relationship between the share
of children placed with kin and payment to kin by licensing options. Fitted lines of linear
regressions of the relationship are also provided. To control for unobserved state hetero—
geneity that remain fixed over time, all the values are measured in changes between two
consecutive (policy) years. The figure further illustrate that on average, changing toward
more (less) stringent licensing is mostly accompanied by higher (lower) subsidies. However,
there seems to be a weak, if any, association between kinship care use and payment, regard-
less of the licensing category. To more rigorously check their relationship, regression-based

analysis will be conducted below.

4 Reexamining Previous Work

The first empirical exercise is to use more recent data to replicate the main work by Doyle
and Peters (2007) (DP) and Duncan and Argys (2007) (DA), two of the first studies to
measure the effects of foster care subsidies on the placement of foster children. Although

they both find significant effects of foster care payments, their results are not directly

16

comparable due to different sample construction and empirical specifications. So this
section will update the two studies respectively to check the robustness of their findings.

Table 1.2 reports the main results published in DP and the replicated estimates for
a more recent. time period. Their main specification is an ordinary least squares (OLS)
regression of children in kinship and non-kin foster families (per 1,000) on a quadratic in
the foster care payment, controlling for year and state fixed effects. The coefficients from
the fixed-effects model (DP, Table 3), which is estimated using state panel data from the
Voluntary Cooperative Information System Survey (VCIS) over 1987-1995, are shown in
column 1. The estimates indicate that the effect is close to zero near the mean of the
subsidy. At the sample average of $260, a $100 increase in the foster care subsidy would
increase the rate of foster children by merely 0.03 per 1,000. The replication constructs
a state panel based on the AFCARS data of 1997-1999, 2001-2002, and 2005 to estimate
DP’s model.21 Column 2 restricts the sample to include the same 37 states as in DP’s
sample,22 and column 3 extends to all available (49) states. In either case. the coefficients
on foster care payment turn out. not to be statistically different from zero, although the
marginal effect (also evaluated at $260) appears to be much larger.

One limitation to DP’s data is that their dependent variable counts all children in foster
care no matter when they entered the system, which implies a questionable assumption
that current subsidy could affect foster children placed years before. To capture the subsidy
effect more accurately, it is more appropriate to include only children who entered foster
care during the current year. This is done in column 4 of Table 1.2, which presents the

preferred estimates based on foster care entries. The point estimates suggest that a $100

 

21The AF CARS data of 1998 and 2002 are not included in the main analysis due to lack of
kinship policy information, but data on foster care payments are available for these two years.
22Special thanks to Joseph Doyle and Elizabeth Peters for kindly providing their VCIS sample.

17

increase in foster car payment would increase the rate of children entering family homes by
0.29 per 1,000, approximately 10% of the sample mean. However, similar to those shown
in columns 2 and 3, the estimates are not statistically significant.

Two main factors may contribute to the findings of an insignificant effect of the foster
care subsidy for the more recent time period.23 First, the VCIS and AFCARS datasets
are not thought to be comparable, partly because some states might be inconsistent in
reporting foster children when switching from the voluntary survey to the new federal
requirements— the AFCARS system. Second, as pointed out by DP, the earlier years
(especially the late 1980s and early 1990s) were characterized with much faster growth in
foster care (which also implies a larger variation in the dependent variable) and greater
concerns about a shortage of foster parents, thus making it. more likely to trace out a
significant relationship between the subsidy and foster care supply?4

While DP’s analysis does not distinguish between kinship and non-kin care, DA use a
micro-level sample from the 1998 AFC ARS to examine how the foster care payment affects
the specific placement. types of children who entered foster care during that year. Table
1.3 first repeats DA’s main analysis and then extends their sample to include more years
and states.25 To begin with. column 1 reports DA’s full-sample estimates (DA, Table 5),
which suggest that increasing foster care payments reduces the likelihood of placement in
group homes, with more children going to non-kin families. Then column 2 reconstructs

DA’s sample and closely replicates their results, although the magnitudes appear somewhat

 

2“”‘DP also try including 1999, 2000, and 2002 AFCARS data into their sample and find that
the significant effect of the subsidy stems solely from the earlier VCIS period.

24Although results not shown. DP recognize (p.347) the loss of precision in coefficient point
estimates after excluding Maryland, the state with the highest subsidy rate but a relatively low
placement rate. Dropping Maryland does not change the replication results here.

25The table reports the marginal effects of a $100 increase in the foster care payment on child
placement, which are calculated from multinomial logit regressions. To conform with DA, all
Standard errors are clustered by state/ age group instead of by state (as in this paper).

18

smaller. Note that although their sample is cross-sectional, DA are able to include state
effects by linking children to age-specific foster care payments (for 2, 0, and 16 years).
Exploiting the within—state variation in subsidies across ages may to some extent correct
the bias caused by unobservable state heterogeneity. but. the bias could still remain if there
exists some age-specific l‘ieterogeneity as well. While a cross-sectional sample is not able to
address this concern, a straightforward way is to introduce more years of data to control for
any time-invariant state heterogeneity. Thus. columns 3 and 4 expand the 1998 sample to
include four more years (maintaining the same states), and reestimate the model without
and with year effects. Both the magnitudes and significance of the estimated effects of
foster care payments are reduced. suggesting that DA’s single-year estimates could be
subject to omitted variable bias. The weaker effects of foster care subsidies persist after
states not in DA’s sample are further included,26 as shown in the last column.

In summary, in contrast with the findings of DP and DA, the updates of their work
show weaker effects of foster care payments on either the total amount of children placed
in foster care or the specific placement settings. Although the replication follows their
empirical models to make results comparable, the specifications in both studies could be
problematic because, as argued earlier, foster care payment. is certainly not a good measure
of the subsidy paid to kin. Given that in many states kin are treated differently from
non-kin foster parents, it is necessary to explicitly include economic incentives for kinship

caregivers in the research, which is the theme of the following section.

 

26Besides the states that did not submit the AF CARS data in 1998, additional six states are
dropped by DA for minor reasons. These states are all included here.

19

5 Estimation

5. 1 Empirical Model

Before presenting the estimation results, the empirical framework is first outlined. Foster
care placement can be modelled in a random utility framework. From a caseworker’s
perspective, the problem is to choose a setting most beneficial to the child based on a full
assessment of the child’s circumstances and the availability of possible alternatives. Given
three placement options (denoted by j: kinship family, non-kin family, and group home), a
caseworker would place child 2' into the one that maximizes the child’s utility Uz’j- Suppose

the indirect utility of placement. alternative j is given by
if I .

where P denotes a vector of variables that measure the economic incentives for foster par-
ents, X denotes observed (by the researcher) child characteristics, and e is an unobserved
component. The subscript 3 indicates that the incentive variables are defined at the state
level, and all variables in P and X can be time-varying when multiple years of data are

used. A caseworker will make choice j when
Uij > Uik V k # j. (2)

The key interests lie in how licensure difficulties and payments to kinship and non-
kin caregivers affect the willingness of kin and non-kin parents to provide care. For this
purpose, the empirical model will estimate the relationship between the economic incentives
and the placement of children with family homes. As the placement is jointly determined
by demand and supply factors if the market clears, to regard the estimated relationship

as a supply curve, it is assumed that. there exists excess demand and thus the variation

20

in family homes comes from the supply side. This identifying assumption seems plausible
given concerns about shortages of foster parents (which have pushed states to seek more
use of kinship care) and the common use of group homes as an alternative of last resort
for children who cannot find family homes. Historical evidence also suggests that increases
in subsidies due to federal funding aimed to partially alleviate excess demand (US DHHS,
2000), reflecting a movement along the upward sloping supply curve.

To conduct the regression analysis. a standard multinomial logit (MN L) model is es-
timated. The model fully includes the state policy variables and child controls listed in
Table 1.1, as well as year and state fixed effects. State unemployment is also included
to allow for business cycle effects. The unemployment rate has been previously used as
an economic condition variable that may affect the demand for foster care services (see,
e.g., Swann and Sylvester, 2006; Doyle and Peters, 2007), but it can also be a supply-side
factor that captures the opportunity costs to fostering children. The year indicators are
intended to pick up changes in foster care placement. that are constant across states but
vary over time. The state effects attempt to capture unobserved heterogeneity that are
assumed to be common within a state over time, such as child protection attitudes toward
and preferences over different types of care, or other long-established child welfare policies
and practices. The standard errors are corrected for clustering at the state level to allow

for dependence across children within the same state and over time.

5.2 Effects of Economic Incentives

Table 1.4 presents the main estimation results. The marginal effects calculated from the
MNL model are reported. The findings in Table 1.4 first indicate that. relaxing licensing

requirements for kin increases the use of kinship care. Children in states of waived licensure

21

or separate approval have a higher probability (about 5 percentage points higher) of being
placed with kin than those in states of full licensure (the omitted category), and the increase
in kinship care both comes from the decrease in non-kin homes. Given that one-quarter
of children in the sample are placed with kin, the estimated effect on kinship homes is
not trivial. These results suggest. that easing the licensing standards may greatly reduce
the costs for kin to acquire a license, and thus help to more easily find kinship homes for
children who would otherwise have been placed in unrelated families.

On the other hand, Table 1.4 also demonstrates that increasing payments to foster
parents has little effect on the placement of children. For the two payment variables, the
point estimates suggest that higher kin payments would have more children placed into
kinship homes and less into non-kin or group homes, and higher foster care payments would
have more children placed into both kinship and non—kin families and less into group homes.
Nonetheless, most of the coefficients on kin payment and foster care payment are small in
magnitude and statistically insignificant at the ten percent level (except for the coefficient
on foster care payment for group home), implying minimal effects of both subsidies.

Interestingly, the estimates of unemployment rate suggest a statistically significant
effect. In particular, a one percentage point increase in the unemployment. rate is associated
with a 2.7 percentage point increase (s.d. = 0.013) in the use of kinship care, which comes
from almost. equal reductions in both non-kin care (0.012, s.d. = 0.013) and group home
(0.015, s.d. = 0.007). In other words, it appears that kinship caregivers who are faced with
worse employment opportunities are more likely to provide foster care services, though this
is not the case for non-kin parents.

The child covariates, though not reported, show the similar patterns as observed in
Table 1.1. In general, younger children, African Americans, and children removed for

22

the reason of abuse or neglect all have a higher probability of being placed in kinship
care. Meanwhile, disabled children and those who have been removed because of parental
incarceration are more likely to be placed with non-kin foster parents. Moreover, older ages
and removal resulting from own physical or behavioral problems are significantly associated
with more use of group homes. The coefficients on other characteristics (such as gender and
family structure of birth family) are either small in magnitude or statistically insignificant.

The foster care placement discussed so far always refers to a child’s most recent place-
ment arrangement, which is the only placement setting observed in the AFCARS data.
But as over 40 percent of the children in the sample experienced more than one placement,
it is quite possible that some of them had switched between different types of care since
the initial placement upon entry into foster care.- However, this may not be an important
caveat when interpreting the main results. C onceptually, learning the effects of subsidies
on the initial placement may be less appealing, because it may take time or even a few
trials for caseworkers to find the home best suited for the child.27 Thus the current setting
may be a better index of the placement. that has been determined by caseworkers to be
most beneficial to the child?8

Empirically, when separate analyses are conducted for children who kept staying in
their first placement, children who had changed placement at least once, and children who
left foster care within the current year (whose most recent placement was also the final

one), the estimates for these three subgroups (not shown) are all consistent with the main

 

27This happens more often in identifying and recruiting kin, which can be difficult and time-
eonsuming in certain cases (Geen, 2004). For example, sometimes the birth parent is reluctant to
give information about available kin under the false hope that without placement choices, child
welfare agencies will be unable to remove the child. Even when kin are identified, they may not
qualify or may need time to complete licensing requirements.

28One may reasonably argue that children can still change placement later, particularly for
those who have just entered foster care and are in their first placement. Excluding very recent
entrants (using arbitrary cutoff of 1, 2, or 3 months) does not. affect the results.

23

results. While these estimates might be contaminated by selection problems, they continue
to suggest. that more flexible licensing standards for kin increase the use of kinship care
(the point. estimates are slightly larger in magnitude for the first group and smaller for the
latter two groups), and that the effects of foster care subsidies are small and statistically
insignificant.

5.3 Leads and Lags of Economic Incentives

To identify the effects of licensing flexibility and subsidies on foster care placement. as the
true policy effects, it should be the case that states adjusted their policies independent of
factors that may directly affect the placement (and are also unobservable to researchers).
Although this cannot be directly tested, one indirect approach is to include policy leads
in the regression. The leads should have little effect on foster care placement if the policy
changes were implemented by a random set of states.

However, the results in Table 1.5 do suggest some evidence that the policy changes
might be endogenous. Columns 1-3 show that leads of separate approval and kin payment
appear to have significant effects on kinship homes, and that both the magnitudes and
significance of the marginal effect estimates of contemporaneous licensing measures are
reduced (compared to the main results in Table 1.4). The findings suggest either a feed-
back effect from more use of kinship care to the implementation of more flexible licensing
standards toward kin or some omitted state heterogeneity that is correlated with both fos-
ter care outcomes and policy changes. For wl’iatever reasons, given the estimates of leads
shown here, one needs to be cautious when interpreting the estimates of contemporaneous
variables as the true effects of state policies.

Furthermore, to check how quickly foster parents respond to policy changes, columns

24

4—6 in Table 1.5 report the estimates of a model including lags of state policy changes.
The lags of separate approval and payment variables suggest some lingering effects, and
the effect of the lag of foster care payment appears to be smaller and less precisely esti-
mated than that of the lag of kin payment. Given that the contemporaneous subsidies are
not statistically significant, the results imply that changes in payments may not become

effective immediately.

6 Conclusions

Despite a substantial amount. of variation across states in the use of different types of care
for foster children. little is known about how economic incentives affect these types. This
paper goes beyond previous literature by explicitly taking into account that many states
license and subsidize kin differently than non-kin foster parents, and constructing measures
of economic incentives for eligible kin based on state-specific kinship policies. Linking
policy data to micro—level data of children entering foster care, the paper finds that relaxing
licensing standards for kin (hence lowering their costs to meet licensing requirements) leads
to more use of kinship care and less use of non—kin care, but neither kin payments nor foster
care payments have detectable effects on foster care placement. However, further analysis
of the leads of state variables indicates that policy changes are likely to be endogenous,
suggestng some caution in the main interpretation.

Several reasons may explain the little responsiveness to foster care subsidies found
here. First, it may simply reflect the fact that most foster parents are not motivated by
monetary incentives to offer services. Second, the slow adjustment of real subsidies over
time may generate too little variation to provide meaningful estimates. Third, it could also

be the case that the effects of changes in subsidies are long run rather than immediate, as

25

suggested by the analysis of policy lags.

Finally, another possible reason could be the low rates of receipt of financial assistance,
especially among kinship caregivers. While they must obtain a license in order to take
care of the child, some kinship families do not necessarily receive financial assistance,
even though most of them are eligible. Based on data from the 2002 National Survey of
America's Families, Murray et al. (2004) finds that over 30 percent of eligible children
in kinship foster care do not. receive any kind of payment from states. Some kin may
assume that the placement will be short term and they can meet the child’s needs without
assistance. Some may not be well informed of the assistance they can receive. Some may be
reluctant. to claim payments in fear of too much involvement of child welfare agencies, and
some may even refuse assistance because of the burden it places on birth parents (many
states require birth parents to reimburse the state for placement costs). In any case, low
levels of payment receipt. may call for a need to change policy and enhance outreach efforts.
States need to ensure that the caregivers, whether kin or non-kin foster parents, have the

resources they need to provide high-quality care.

26

Figure 1.1: Number and Rate of Foster Children, 1985-2007

   

         

  

é — 2
§ 8.081 675737'27'1706967_c°
68483 5 6 '7552545 3 195175145094 6 _ co

:35; it ~ _ o

 

 

 

T l |
1995 2000 2005

Number (in 1,0005)
———0— Rate (per 1,000)

 

 

Sources: 1985-1997: Trends in the Well-Being of America's Children and Youth (US DHHS. 1999).
1998-2007: The AFCARS Reports (US DHHS. 2006. 2008).

27

Figure 1.2: Changes in Kinship Foster Care Entries and Payments

 

 

 

 

 

 

All Licensing unchanged
0 0 o
O! ..
. O
.— - 0 .. o. . ‘ . .,
O - C O . . 0 .
T ‘ e V. ‘.
N .l ‘ 0
More stringent licesning Less stringent licensing
o! _, O
. e
,_ d e
, . e . . o .
M
o ‘ . ‘ O Q .0 . ‘o\*
v- . C
I T C
“l d O
-200 -100 O 100 200 -200 -100 0 100 200
Changes in payment to kin
0 Changes in share of kinship entries —— Fitted values

 

 

 

Graphs by changes in licensing options

28

Table 1.1: Descriptive Statistics: AFCARS Sample

 

Placement setting

 

 

Full sample Kin Non-kin Group home
Variable ( 1) (2) (3) (4)
Number of children 826,775 215,366 41 1,380 200,029
Full licensure 0.294 (0.455) 0.217 (0.413) 0.302 (0.459) 0.358 (0.479)
Waived licensure 0.199 (0.399) 0.154 (0.361) 0.223 (0.416) 0.198 (0.399)

Separate approval

Foster care (FC) payment
Kin payment

Male

Non-Hispanic white
Non-Hispanic black
Hispanic

Age when placed
Diagnosed disability

Removed because of
abuse or neglect

Removed because of
child problem

Removed because of
parent incarceration

Age of pre—removal
caretaker

Pre-removal caretaker:
single parent

0.507 (0.500)
477.8 (89.8)
369.4 (147.7)
0.513 (0.500)
0.468 (0.499)
0.288 (0.453)
0.194 (0.395)
8.31 (5.77)
0.126 (0.332)

0.647 (0.478)

0.192 (0.394)

0.050 (0.217)

33.8 (9.53)

0.629 (0.483)

0.628 (0.483)
474.7 (88.3)
345.7 (142.2)
0.486 (0.500)
0.422 (0.494)
0.327 (0.469)
0.210 (0.408)
6.57 (5.00)
0.091 (0.288)

0.778 (0.415)

0.061 (0.240)

0.055 (0.227)

31.6 (8.80)

0.629 (0.483)

0.475 (0.499)
476.6 (90.9)
370.6 (148.4)
0.488 (0.500)
0.481 (0.500)
0.279 (0.449)
0.186 (0.389)
6.90 (5.44)
0.124 (0.330)

0.699 (0.459)

0.127 (0.333)

0.058 (0.234)

32.9 (9.3)

0.625 (0.484)

0.444 (0.497)
483.8 (88.8)
392.4 (148.4)
0.592 (0.492)
0.489 (0.500)
0.263 (0.440)
0.194 (0.395)
13.10 (4.43)
0.167 (0.373)

0.400 (0.490)

0.468 (0.499)

0.027 (0.162)

38.7 (9.1)

0.641 (0.480)

 

Notes: Stande deviations are shown in parentheses. Payments are in 2005 dollars. The sample includes
children under 18 who entered foster care in fiscal years of 1997, 1999, 2001, and 2005. Children in pre-
adoptive homes, trial home visits, or supervised independent living are excluded. Nevada is dropped for

missing placement information. '

29

Table 1.2: OLS Estimates of the Effects of Foster Care Payment: State-Level Data
Doyle and Peters
(2007) published results
(VCIS 1987-1995)

AFCARS (1997, 1998, 1999, 2001, 2002, 2005)

 

 

 

DP’s 37 states A1149 states A1149 states
(1) (2) (3) (4)
Children in family Children in Children in Children
(kinship and non-kin) family homes family homes entering
Dependent variable homes (per 1,000) (per 1,000) (per 1,000) family
homes (per
1,000)
Mean (and s.d.) of dep. 3.71 4.71 5.08 2.98
var. (2.24) (1.84) (2.38) (1.25)
Mean (and s.d.) of EC 258 266 278 278
payment (in 1987 dollars) (66) (62) (64) (64)
FC payment 0032*" -0.023 0.028 -0007
(0.009) (0.018) (0.044) (0.008)
FC payment squared -0.061*** 0.049 -0.049 0.019
(divided by 1,000) (0.015) (0.033) (0.087) (0.015)
Marginal effect ofa $100 0.028 0.248 0.252 0.288
increase in PC payment
(evaluated at $260)
State fixed effects Yes Yes Yes Yes
Year fixed effects Yes Yes Yes Yes
R-squared 0.94 0.86 0.87 0.87
Sample size 200 152 204 204

\

Notes: *, "'*, and *” represent significance levels of 10, 5, and 1 percent. Standard errors clustered by state
are shown in parentheses. Column 1 reports the results of Doyle and Peters (2007, column 3 of Table 3) for a
specification that includes only state and year fixed effects, and Columns 24 use the same specification.

30

Table 1.3: Marginal Effect Estimates of the Effects of Foster Care Pament: AF CARS

Marginal effects from multinomial logit model

 

 

 

Duncan and R lication of Extended (3) lus ear (4) plus
Argys (2007) ep years for (2) p y additional
. Duncan and . fixed effects
published Ar w1thout year states
gys
results (2) fixed effects (4)
(1) (3) (5)
Sample year 1998 1998 1998, 1999, 1998, 1999, 1998, 1999,
2001, 2002, 2001, 2002, 2001, 2002,
2005 2005 2005
Number of 34 34 34 34 49
states
Sample size 89,767 82,573 433,776 433,776 624,791
Kin -0.034*** -0.020* 0.011“ -0.001 0.012"
(0.014) (0.012) (0.005) (0.005) (0.005)
Non-kin 0.105*** 0056*" 0.000 0.008 -0.007
(0.022) (0.020) (0.005) (0.006) (0.006)
Group -0.07l*** -0.037*** -0.011*** -0.007* -0.004
(0.020) (0.016) (0.004) (0.004) (0.005)

 

Notes: *, **, and *** represent significance levels of 10, 5, and 1 percent. Standard errors clustered
by state/age group are shown in parentheses. Each column represents one regression and reports the
marginal effect (evaluated at the sample averages) of a $100 (in 1998 dollars) increase in foster
care payment on foster care placement. Column 1 reports the results of Duncan and Argys (2007,
row 1 of Table 5) for a specification that includes indicators for age, male, non-Hispanic black,
Hispanic, other race, disability, parents’ rights being terminated, reasons for removal (parental
abuse or neglect, behavioral problems of the child, or parental incarceration), and state fixed
effects. Duncan and Argy’s sample is restricted to children aged 16 and younger who entered foster
care for the first time. Columns 2-5 apply the same regression specification and sample restrictions.

31

Table 1.4: Estimates of the Effects of Economic Incentives: AFCARS

Marginal effects from multinomial logit model

 

 

Kin Non-kin Group
(1) (2) (3)
Waived licensure 0052*“ -0.078*** 0.026
(0.017) (0.016) (0.016)
Separate approval 0.045*** -0.054* 0.010
(0.020) (0.029) (0.015)
Kin payment (in S 100) 0.007 -0.005 -0.002
(0.017) (0.014) (0.007)
FC payment (in 8100) 0.031 0.008 -0.039***
(0.020) (0.022) (0.014)
Unemployment 0.027** -0.012 -0.015**
(0.013) (0.013) (0.007)
Pseudo R-squared 0.20
Sample Size 826,775

 

 

Notes: *, **, and *** represent significance levels of 10, 5, and 1 percent. Standard errors clustered
by state are shown in parentheses. Marginal effects evaluated at the sample averages are reported
The child controls include age, age squared, age cubed, indicators for male, non-Hispanic black,
Hispanic, other race, disability, parents’ rights being terminated, reasons for removal (parental
abuse or neglect, behavioral problems of the child, or parental incarceration), pre-removal family
structure (married couple, unmarried couple, or single parent), and age of the principal caretaker

prior to removal. Both year and state fixed effects are included. Full licensure is the omitted

licensing category.

32

Table 1.5: Estimates of the Leads and Lags Effects of Economic Incentives: AFCARS

 

Marginal effects from multinomial logit model

 

 

 

Leads Lags
Kin Non-kin Group Kin Non-kin Group
(1) (2) (3) (4) (5) (6)
Waived licensure -0.006 -0.024* 0.030 0.025 -0.058*** 0.033“
(0.021) (0.015) (0.023) (0.017) (0.016) (0.014)
Separate approval 0.015 -0.012 -0.003 0.025 -0.038** 0.013
(0.017) (0.021) (0.020) (0.018) (0.024) (0.012)
Kin payment (in $100) 0.026 -0.015 -0.01 1 0.004 -0.003 -0.001
(0.022) (0.019) (0.008) (0.014) (0.012) (0.007)
FC payment (in $100) 0071*" -0.052*** -0.019 0.033 0.014 -0.046***
(0.020) (0.020) (0.017) (0.016) (0.019) (0.014)
Waived licensure lead/lag 0.002 -0.016 0.014 -0.020 0.004 0.016
(0.030) (0.026) (0.021) (0.024) (0.020) (0.015)
Separate approval lead/lag 0058*" -0.017 -0.041** 0.043 -0.086"* 0043*"
(0.018) (0.016) (0.020) (0.025) (0.021) (0.009)
Kin payment lead/lag 0.035” -0.020* -0.016 0050*" -0.034*** -0.016"”'I
(in $100) (0.014) (0.012) (0.012) (0.010) (0.008) (0.007)
FC payment lead/lag -0.022 0.035 -0.013 -0.014** 0.012 0.002
(in $100) (0.026) (0.023) (0.020) (0.007) (0.007) (0.007)
Pseudo R-squared 0.20 0.21
Sample size 570,619 718,104

X

Notes: *, *"‘, and *** represent significance levels of 10, 5, and 1 percent. Standard errors clustered by state
are shown in parentheses. Both regressions include the full child controls as specified in Table 1.4, plus both

year and state fixed effects.

33

‘ Appendix

I. Background of Foster Care Placement
Foster care is full-time substitute care for children removed from their parents
or guardians and for whom the state has responsibility. Foster care usually begins
when a mandated reporter or concerned citizen makes a report of abuse or neg-
lect to a state child welfare agency. Then the agency launches an investigation to
find whether abuse or neglect has occurred and assesses the risks to the child if so.
If the case is substantiated, based on the risk assessment, the agency determines
whether the child can remain safely at home with supervision or should be
removed from home (and enter foster care).

When the investigation indicates that the child is at high risk of subsequent
abuse or neglect, the child welfare agency petitions the court recommending the
removal of the child from his or her parents. This petition initiates a series of ju-
dicial hearings for the court. to determine whether the child has been abused or

neglected and whether the child must. be removed from home. Generally the ju-
dges’ decisions are largely based on the child welfare agency’s recommendation.
C)‘tice the court orders to remove the child, the child becomes formally involved
‘Vi th the juvenile or dependency court system, and the child is considered in state

C31.13t0dy.
Upon the court order to remove the child from home, the child and his or her

fa Inily are assigned a caseworker from the child welfare agency. The caseworker

34

is required to develop a case plan detailing an initial placement plan, a reuni-

fication plan (including visitation schedules and a target date for returning home),

an alternative permanency plan should the reunification plan fail, and other types
of services that the child and the family may receive.

The placement. plan specifies where a child will receive foster care. Federal re-
gulations clarify that health and safety are the paramount considerations when
any placement decision is made, and require that the case plan describe how the
state will achieve a safe placement in the least restrictive, most family-like setting
in close proximity to the child’s parents. Following these guidelines, the case-
worker seeks for a placement arrangement that best serves the interests and
special needs of the child. In most cases, based on the availability of homes and
the child’s individual circumstances, foster parents are matched with foster child-
I‘en through negotiation between the caseworker and the potential foster care pro-
Vider. The usual placement options include kinship family home, non-kin family
home, and group home care. (Also see details of the placement decision-making in

Section 2.1.)

11. Data Sources

Table 1 .6 provides the sources of the data used in the paper.

HI- Vafiation in Licensing Policies and Subsidies

35

 

The policy variables regarding how states license and subsidize kinship foster
parents are defined in Table 1.7. Table 1.8 shows the distribution of licensing
and payment policies across states and over years (see Section 3.1). The variation
in subsidy amounts (in both levels and changes) is illustrated in Figure 1.3 (see

Section 3.1).

36

Changes in foster care payment

Foster care payment (payment to non-kin)

Figure 1.3: Foster Care Payments and Kinship Payments

 

 

 

 

 

 

1997 1999
8 4 '
e - ' ‘ . °
0 o . .9 ° 0 .3.
O 9 O O .
§_l‘.. '0‘.”.
O 0 ~
0
o —1
N
2001 2005
o
8 - o
co 0
. C
o
gl’ .0 O 0’ . . 9 I.
O. . . . ./ ' O .
o o '00 ' so ’I.
8‘ ~ 0 . O. Q. Q C
’0' o O .
O
o —l
N I I I I T I I I I I I I I I I I
100 200 300 400 500 600 700 800 100 200 300 400 500 600 700 800
Payment to kin
Graphs by year
1997-1999 1999-2001
e
O
8 .1
o
8 _ o
o“. .2 ’ . . .0 $ 500000 0
D . 0
g _
"’ l
C)
“'. I I I I I I I
-300 -200 -100 0 100 200 300
2001-2005
C)
O
N o
O o
D
g 0 O. O
O . .
8 Jo. ' °
6 e
O
9‘

I r I I

I l I
~300 -200 -100 0 100 200 30
Changes in payment to kin

Graph 8 by year

37

Table 1.6: Data Sources

 

 

 

 

Data Source Year
Adoption and National Data Archive on Child Abuse and 1997-2005
Foster Care Neglect, Cornell University (originally
Analysis and collected by the Children’s Bureau, U.S.

Reporting DHHS)

System

(AFC ARS)
State kinship Urban Institute survey reports (Boots and 1997, 1999, 2001
foster care Geen, 1999; Leos-Urbel et al., 2000; Jantz et
policy al., 2002)
State fact sheets for grandparents and other 2005
relatives raising children (AARP Foundation et
al., 2005) (http://www.gu.org[factsheets.asp)
Foster care Boots and Geen (1999) 1996
monthly
maintenance rate
Child Welfare League of America National 1999, 2000,
Data Analysis System 2002, 2004
(http://ndas.cwla.org/home.asp)
AFDC child- Geen and Waters (1997) 1995
only benefit
AFDC/TANF University of Kentucky Center for Poverty 1995-2005

benefit for 2-
person family

 

Research
(http://www.ukcpr.org/Availab1eData.aspx)

 

Notes: For some states offering few details on kinship policies, the author communicates with
state child welfare contacts that are listed on the fact sheets.

38

gTable 1.7: Definitions of State Kinship Licensing and Payment Policies

 

 

Variable Licensing option Payment option
Full Kin are assessed based on the same standards Foster care
11' censure as non-kin foster parents. No standards are Other
waived for kin that cannot be waived for non-
kin parents.
Waived Kin are assessed based on the same standards Foster care
\icensure as non-kin foster parents, but some non-safety TANF child-only
standards can be waived on a case—by—case Other
basis.
Separate Kin are assessed based on different standards Foster care
approval than those for non-kin foster parents. Usually TANF child-only
these standards are less stringent than those for Other
non-kin.

 

Notes: A few states provide foster care payment only to kin caring for Title IV-E eligible
children and TANF to others. The most commonly waived standards are space and parent
training requirements. States may also waive age, income, or other requirements as long as
they do not threaten the safety of the child. Kin assessed by separate standards are referred to
as “approved,” “unlicensed,” or “uncertified” by different states. Some states just require a
minimum level of home study and background check to approve a kinship home. Some states
provide kin with a rate less than foster care payment but greater than TANF .

39

 

Table 1.8: Summary of State Kinship Licensing and Payment Policies

 

Number of states

 

 

 

 

Full . .
licensure Waived licensure Separate approval

Y Changed Foster Foster T ANF Other Foster Othe
7 E care care care r
l 997 - 9 9 1 2 6 18 6
\ 9 99 14 1 1 6 0 3 4 20 7
200 l 19 15 12 2 2 2 15 3
2005 19 24 8 0 0 1 12 6

 

Notes: See definition of policy variables in Table 1.7. California and Oregon provide foster care
payment only to kin caring for Title IV-E eligible children and TANF to others.

40

References

AARP Foundation, Brookdale Foundation Group, Casey Family Programs, Child
Welfare League of America, Children’s Defense Fund, and Generations United.
Sta te Fact Sheets for Crandparen ts and Other Relatives Raising Children.

h t. t p: //www.gu.org/factsheets.asp, 2005.

Boots, Shelley W. and Rob Geen. “Family Care or Foster Care? How State
Policies Affect Kinship Caregivers.” New Federalism: Issues and Options for
States No. A-34. Washington DC: Urban Institute, 1999.

Campbell, Claudia and Susan Whitelaw Downs. “The Impact of Economics
Incentives on Foster Parents.” Social Service Review 61 (1987): 599-609.

Center for Law and Social Policy (CLASP) and Children's Defense Fund. State
Fact Sheets on Child Welfare Fun ding.
htt p : / / claspergf publications,-*"StateFactSheetsOnChildVVelfareF unding06.ht m,

2006 .

Chamberlain, Patricia, Sandra Moreland, and Kathleen Reid. “Enhanced Services
and Stipends for Foster Parents: Effects on Retention Rates and Outcomes for
Children.” Child Welfare 71 (1992): 387-404.

Cuddeback, Gary S. “Kinship Family Foster Care: A Methodological and
Substantive Synthesis of Research.” Children and Youth Services Review 26

(2004).- 623-39.

Doran, Lee and Lucy Berliner. “Placement Decisions for Children in Long-Term
Foster Care: Innovative Practices and Literature Review.” Olympia, WA:
Washington State Institute for Public Policy, 2001.

Doyle, Joseph J. “Can’t Buy Me Love? Subsidizing the Care of Related Children.”
Journal of Public Economics 91 (2007): 281-304.

Doyle, Joseph J. and H. Elizabeth Peters. “The Market for Foster Care: An
Emplrical Study of the Impact of ‘ Foster Care Subsidies.” Review of Economics of

Households 5 (2007): 329-51.

Duncan, Brian and Laura Argys. “Economics Incentives and Foster Care
Placement .” Southern Economic Journal 74 (2007): 114-42.

41

Geen, Rob. “The Evolution of Kinship Care Policy and Practice.” The Future of
Children 14 (2004): 130-49.

Geen, Rob and Shelley Waters. “The Impact of Welfare Reform on Child W'elfare
Financing.” New Federalism: Issues and Options for States No. A-16. Washington

DC: Urban Institute, 1997.

Harden, A., R. Clark, and K. Maguire. Informal and Formal Kinship Care.
Volume I: Narrative Reports. Washington, DC: US. Department of Health and

Human Services, 1997.

Ingram, C. “Kinship Care: From Last Resort to First Choice.” Child welfare 75
(1996): 550-66.

J antz, Amy, Rob Geen, Roseana Bess, Cynthia Andrews, and Victoria Russell.
“The Continuing Evolution of State Kinship Care Policies.” Assessing the New
Federalism Discussion Paper No. 02—11. Washington DC: Urban Institute, 2002.

Kang, Hyun—ah. “Caregiving Environments of Kinship Care: Literature Review.”
The Children and Family Research Center, School of Social Work, University of

Illinois at Urbana-Champaign, 2003a.

--. “VVell—Being Outcomes of Children in Kinship Care: Literature Review.” The
Children and Family Research Center, School of Social Work, University of

Illinois at Urbana-Champaign, 2003b.

Kusserow, R. Using Relatives for Foster Care. Washington, DC: US. Department
Of Health and Human Services, Office of Inspector General, 1992.

Loes-Urbel, Jacob, Roseana Bess, and Rob Geen. “State Policies for Assessing
and Supporting Kinship Foster Parents.” Assessing the New Federalism
Discussion Paper. Washington DC: Urban Institute, 2000.

Malm, Karin and Roseana Bess. “Identifying and Recruiting Kin to Act as Foster
Parents-” In Kinship Care: Making the Most of a Valuable Resource, edited by
Rob Geen. Washington DC: Urban Institute Press, 2003.

Murray, Julie, Jennifer Ehrle Macomber, and Rob Geen. “Estimating Financial
support for Kinship Caregivers.” New Federalism: National Survey of America ’s

Famzlzes. N o. B—63. Washington DC: Urban Institute, 2004.

Paxson, C3}]ristina and Jane VValdfogel. “Work, Welfare, and Child
Maltreatment.” Journal of Labor Economics 20 (2002): 435-74.

42

 

——. “\Nelfare Reforms, Family Resources. and Child lVIaltreatment.” Journal of
Policy Analysis and rllanagement 22 (2003): 85-113.

Shlonsky, AR. and J .D. Berrick. “Assessing and Promoting Quality in Kin and
Nonkin Foster Care.” Social Service Review 75 (2001): 60-83.

Simon, Julian. “The Effect of Foster Care Payment Levels on the Number of
Foster Children Given Homes.” Social Service Review 49 (1975): 405-11.

Swarm, Christopher A. and l\=‘lichelle Sheran Sylvester. “The Foster Care Crisis:
V’Vhat Caused Caseloads to Grow?” Demography 43 (2006): 309-35.

Templeman, Amy Jantz. “Licensing and Payment of Kinship Foster Parents.” In
Kinship Care: llfaking the .Most of a Valuable Resource, edited by Rob Geen.
Washington DC: Urban Institute Press, 2003.

Testa, MF. and N. Rolock. 1999. “Professional Foster Care: A Future Worth
Pursuing?” Child Welfare 78 (1999): 109-24.

(LS. Department of Health and Human Services, Administration on Children,
Youth and Families. Child Welfare Outcomes 1998: Annual Report.
http: / /www.acf.hhs.gov;"programs/Cb,r’pubs,icw098/cw098.pdf, 1998.

--. Trends in the W’ell-Being of America :9 Children (fr Youth, 1999. Washington,
DC: US Government Printing Office, 1999.

——. Report to the Congress on Kinship Foster Care. Washington, DC: US
Government Printing Office, 2000.

-~. The AF CARS Report 1:12. Final Estimates for FY 1998 through FY 2002.
1') t; tp: / /www. acf. hhs. gov?programs] (Tb/stat s _ rescarch/afcars / tar [report 1 2. pdf ,

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~~ - Trends in Foster Care and A (lop tion —F Y 2002-F Y 2007.
h t tp://www.acf. hlisgov; programs/(fl),rstats_rest3a1’clr,./af(.'ars/ trendsO‘Z-U7.pdf,

2008.

43

Chapter 2
One-Child Policy, Fertility, and Divorce

(with Hongbin Li and Junsen Zhang)

44

1 Introduction

Economists and other social scientists have long noticed the sophisticated relationship
between children and marriage stability. As pioneers of the literature, Becker and his
associates (Becker et al., 1977; Becker, 1991) argue that. the existence of children promotes
stable marriages. According to this argument, children increase the benefits of marriage,
because they are marital—specific capital that becomes less valuable to parents should the
marriage dissolve. Children can also be described as the products of stable marriages.
As Becker et a1. (1977) point. out. the possibility of marital dissolution discourages the
accumulation of the marital-specific capital, children. The simultaneity between having
Children and marriage stability makes it an extremely difficult task to empirically establish
causality. Partially because of this difficulty, previous findings on the effect of children
on marriage stability have been mixed. Some document the stabilizing effect. of children,
especially young children, on marriage (Becker et al., 1977; Peters, 1986; Waite and Lillard,
1 991), but others find that children have little to do with enhancing marriage stability
C Harman et al., 1977; Mott and Moore, 1979; K00 and Janowitz, 1983; Jacobsen et al.,
2001).

Two main strands of empirical studies have taken up the challenge of disentangling
the causal link between fertility and divorce. One strand applies complex simultaneous
duration models to solve endogeneity (K00 and Janowitz, 1983; Lillard, 1993; Lillard and
\Naite, 1993; Vuri, 2002; Svarer and Verner, 2004). However, this method may be hard.
to implement, because it requires very specific data sets, and appropriate ii‘istrumental
Variables (IVs) for either fertility or marriage are not usually easy to find. The other

Strand tackles endogeneity by using natural experiments such as twin births (Jacobsen et

45

al., 2001) or sibling—sex composition (Angrist, 2004) to identify fertility.l As twin births
incur an additional unplanned child, and parents of same-gender siblings are more likely to
go on to have an additional child, these instruments allow economists to detect the impact
of the number of children on marital stability. However, both instruments are imperfect,
because a large sample of mothers with twins is not easily available, and the gender of
children is likely to directly influence. the stability of the marriage.

This paper can be distinguished from previous studies in the important way that we
attempt to measure the causal effect of fertility on marriage stability with a new identifying
instrument that is based on the one-child policy in China. Under this policy, which was
introduced in 1979, each family is allowed only one child and parents are heavily fined for
any second or higher-parity births. However, the policy applies only to the Han Chinese.
In contrast, ethnic minority women in China were allowed to have two children until the

end of the 19808 (Hardee-Cleaveland and Banister, 1988; Anderson and Silver, 1995), and
thus the fertility policy for the minorities is essentially a two-child policy.2

The affirmative aspect of the policy provides us with a unique natural experiment in

vvhich to identify its effect on fertility and the causal effect of fertility on marriage stability.
“’0 achieve these by two-stage least squares (2SLS) estimations. In the first stage of the
2 SLS, we measure the effect of the one—child policy on fertility by employing the differences-
ir1~differences (DD) estimator, which exploits the differences in the probability of having
a. second child between the Han. Chinese (treatment group) and ethnic minorities (control

group), both for birth cohorts that are affected by the. policy (post-treatment group) and

\

1Bruderl and Kalter (2001) approach the topic using another IV, a time-varying indicator of

IIlatrital problems based on the responses of individuals to two questions on marital discord.
2Some minority—dominated autonomous regions such as Xinjiang and Tibet may allow minority

Women to have more than two children. See Section 2 for institutional details.

46

birth cohorts that are unaffected by the policy (pre-treatment group). For this purpose,
we use the interaction of the birth cohorts and a Han dummy to identify the exogenous
variability in fertility that can be attributed to the introduction of the one-child policy.
In the second stage, we estimate the effect of fertility on marriage stability by using the
exogenous variation in fertility that is predicted by the DD method in the first stage.
This DD identification strategy is very clean, because we do not have to rely on locality
or individual-specific instruments that are very likely to be correlated with unobservable
determinants of the marriage dissolution.

Drawing on the 1982 and 1990 Chinese Population Censuses, our DD estimations in-
dicate that the one-child policy has had a significant effect on reducing the probability
of second births among the Han Chinese compared to the probability among the ethnic
minorities. The DD estimates are statistically significant for all of the 1946-1970 cohorts,
which are defined as the post-treatment group in our analysis. The average effect for the

post-treatment cohorts is -9.2 percentage points, with the largest effect of -20 percentage
points identified for the 1958 cohort.

To have more confidence in the DD estimates, we need to make sure that they are
11012 mainly picking up the effect of other policy shocks or economic changes. The key
assumption of the DD method is that without the one-child policy, the changes in the
probability of having a second child for the Han and the minorities would have been the
Sarne between 1979 and 1990. If there are other policy shocks or changes in social-economic
Variables in the same period that have affected the fertility behavior of the Han and the
IIlinorities differently. then the DD method may have identified the effect of these policies

Or changes.
To check the robustness of our DD estimates, we first show that the estimated effects

47

only change marginally when we add controls for women’s education and the rural and
provincial dummies. We also test the validity of the key assumption by examining whether
other personal or household decision variables, which may reflect parental preference and
the opportunity costs of children but are not likely to be affected by the one-child policy,
have changed in different ways for the Han and the minorities in the treatment period.
If the DD estimates for these alternative dependent variables are large, then we should
be cautions that our estimates are probably picking up other effects. In general, the DD
estimations for the variables of marriage, first-birth behavior, education, migration, and a
few labor market outcomes suggest that our estimates of the effect of the one-child policy
on the probability of having a second child should not be mainly driven by other factors.

With regards the fertility-divorce relationship, our ordinary least squares (OLS) esti-

mations find a robust negative association between a second birth and the probability of
being divorced in China. However, the ZSLS estimations using the DD estimators as IVs
suggest that having a second child has little, if any. effect on improving marriage stability.
This finding suggests that a simple OLS model tends to overestimate the stabilizing effect
in the presence of simultaneity or omitted variable bias, and having an additional child
ilnposes little causal effect. on irlarriage stability.

This study contributes to the literature of family economics, in particular that which
eXamines family stability and fertility policies. We provide an identifying instrument based
On the affirmative birth control policy in China that has not been used in the literature.
It can potentially be used to break endogeneity in relationships between fertility and other
economic outcomes. In this sense, we contribute to the literature that explores natural

eXperiments in social settings (see. for example, Rosenzweig and \Nolpin (1980 and 2000),
Ashenfelter and Krueger (1994), and Behrman and Rosenzweig (2004)).

48

We are also among the first to use a large national dataset from China to empirically
examine the relationship between fertility and marriage stability. In contrast to the rich
studies based on Western datasets, until recently little research had been done on the
determinants of marriage stability in China,3 even though the crude divorce rate in China
has risen much faster than in most other countries over the past two decades.“ Even the
small body of studies on the fertility—marriage relationship in China simply treat fertility
as an exogenous variable and rely on regional small samples only.5 Thus, the results of
these studies are often unconvincing.

Another important aspect of our study is that the DD method allows us to directly
measure the effect of the one-child policy on fertility. As a rare and probably the largest
social experiment in human history, China’s one-child policy provides a unique opportunity
for researchers to examine the impact of counter—natal policies (Birdsall, 1988).6 Although
the policy has spurred a vast. amount of research, particularly in the field of demography,

no study has been able to directly measure the effect. of the one-child policy on fertility
( Johnson, 1994; Li, 1995; Qian, 1997; Short and Zhai, 1998). In fact, most of these
studies have related the variation in fertility to the variation in the implementation of the

one-child policy across localities, rather than examining the effect of the one-child policy

 

 

3Most studies analyze the pattern or trend of divorce in China, but they are largely descriptive
Without empirical tests of how the divorce rate is associated with socioeconomic eovariates. See
Zeng and Wu (2000) and other studies cited therein.

4Wang (2001) estimates that the crude divorce rate almost tripled in China between 1979 and
1 997.

5An example is Zeng et al. (2002), who investigate how the divorce risk is affected by social
and demographic factors using the In-Depth Fertility Survey data collected from three provinces
in 1985. They confirm that the number of children is negatively correlated with the probability

Of divorce, but their analysis fails to account for the endogeneity of fertility.
6Pro-natal policies, which occur more often, have been much more thoroughly studied. Most

eInpirical work finds that pro-natal policies. such as child subsidies or tax deductions, have a
positive effect on increasing fertility. See, for example, Vi'hittington et al. (1990) and Zhang et
al. (1994).

49

itself. Another problem with these studies is that most have ignored the endogeneity
of the local policy variables. Tougher local implementation of the one-child policy may
be a result of high local fertility, in which case there is a. feedback effect from fertility
to local implementation. Tougher implementation may also be a result of omitted local
In contrast to this

preferences, which affect both fertility and policy implementation.

literature, we identify the effect of the one-child policy itself, and our identification is

based on the central policies.

The remainder of this paper is organized as follows. Section 2 describes the birth

control policy and divorce in China. Section 3 specifies our empirical model and Section 4
describes the data. Section 5 presents the estimation results of the effect of the one-child

policy on fertility, and Section 6 reports the results of the effect of fertility on divorce.

Section 7 concludes the paper.

2 The Birth Control Policy and Marriage Stability in
China '

2.1 The One-Child Policy

China introduced its unique one-child policy in 1979. Under this policy, each couple is
allowed to have only one child. Households are given birth quotas, and they are penalized
for “above-quota births.” Parents with above-quota children are fined for each additional
lJirth. In contrast, parents who comply with the one-child policy receive cash subsidies from
t he government, and their children can also receive free health care such as immunizations.
The overall one-child policy can be classified into two more specific categories: national

and local policies. National policies such as the one—child-per-family policy are applicable

throughout the whole country, but local policies, such as penalties for above-quota births,

50

can vary between regions (e.g., rural and urban) or provinces. The central government
has allowed each provincial government to have its own birth control policies, all based on
national policies, to incorporate local characteristics (CCCPC, 1984). To implement their
birth control policies, local governments are given incentive contracts. These take the form
of fiscal rewards for fulfilling birth targets, and heavy penalties for falling short (Hardee-
Cleaveland and Banister. 1988; Short and Zhai, 1998). Moreover, government officials can
be demoted for allowing too many above-quota births in their communities, which means
that they will lose future income and other benefits associated with government positions.
Local policies, although usually tough, demonstrate great heterogeneity. In particular,
the penalties for above—quota births are much more severe in the urban areas than the
rural areas (Banister, 1987). Urban citizens who violate the policy have to pay fines that
are proportional to their monthly salaries, sometimes as high as 70 percent. They are
demoted or rendered illegible for promotion forever if they work in state—owned enterprises
or institutions, which were the major urban employers in the 19805. The above-quota
Children are not allowed to go to urban public schools, which receive substantial education
subsidies (Short and Zhai, 1998). As a contrast, the only severe punishment in rural areas
is a one-shot fine for above-quota births. Demotions or deprivations of the right to go to
SChool are not as important as they are in urban areas because few rural citizens work for
Staste—owned institutions and public schools are ill-funded in rural China. Even the fine itself
nlay not be very effective in rural areas because many poor farmers cannot afford to pay
it (Li and Zhang, 2008). Because of the difficulty in implementations and the potential for
SOcial unrest, in some rural areas and in certain years the policy has been relaxed to allow
Han people to have second children if the first. is female (Qian, 1997; Hardee-Cleaveland

and Banister, 1988; Chow, 2002).

Other than the urban-rural difference in fertility policies. there is also a large variation
in fertility policy across rural localities. Short and Zhai (1998) find that 41 percent of the
villages in their sample have a strict one—child policy, 43 percent allow a second child if the
first child is a girl, and the remaining 16 percent allow two children without a condition. In
rural areas, fertility fines have been the primary penalty used by local government officials
for above-quota births. Various studies have shown that the fines are heavy and vary
enormously across communities. They range between 20 and 200 percent of a household’s
annual income (Li, 1995; Short and Zhai, 1998).

The unique aspect of the national policy for our research is that it only applies to the
Han. Chinese, and not the minorities, which are normally allowed to have two children
(Hardee—Cleaveland and Banister, 1988; Park and Han, 1990; Anderson and Silver, 1995;
Peng, 1996; Qian, 1997). Although a third child is not allowed for minorities in most
regions, there are some exceptions. For example, in Xinjiang Province, minorities can have
as many as four children. In rural areas of Tibet, there are no restrictions on the number
of children that ethnic minority families can have.

In April 1984, five years after the one-child policy had been implemented for the Han
Chinese, the government stated that there should also be birth control policies for eth-
nic minorities, but that these policies should be less restrictive (CCCPC, 1984; Hardee-
Cleaveland and Banister, 1988). However, to the end of 1988 minority parents were allowed
to have a second child (Deng, 1995). For most of the 19805, they were allowed to have more
than one child in general. This provides a unique natural experiment on the variations of
fertility. In the following analysis, we will make use of the affirmative aspect of the policy
to explore how individual marital decisions are affected by exogenous fertility variations
brought by the national-level policy.

52

2.2 Marriage and Divorce

Divorce was culturally and administratively discouraged in China before the late 1980s.
Culturally, divorce was seen by the Confucian ideology as a very disgraceful matter for
Chinese, particularly for Chinese women (Zeng, 1995). Administratively, the formal proce—
dures for divorce were very time-consuming and hard to complete, even if the divorce was
agreed to by both parties (Li, 1985; Goode, 1993). To obtain a negotiated divorce,7 for
example, both parties were required to obtain certification letters from their work units and
residence committees.8 However, to prevent social instability, the work units and residence
committees were very reluctant to issue such certification. In most cases, they sent staff
members to persuade the couple to stay married, and issued certification only when these
efforts failed. These cultural and administrative obstacles made it quite difficult to obtain
a legal divorce, leading to a relatively low divorce rate in China. As Wang (2001) reported,
the crude divorce rate in China wasfconstantly lower than 0.7 per thousand (population)
by 1990, and despite the steady increase in the 19908, it was still below 1 per thousand by
1998.9

Although the level of the divorce rate in China was rather low, it has experienced
a faster rising trend than most other countries in the past two decades. Wang (2001)
estimates that the crude divorce rate almost tripled between 1979 (0.33) and 1997 (0.97).

Three main factors may explain this upward trend (Zeng and Wu, 2000; Wang, 2001).

 

7Negotiated divorces apply to cases in which both parties provide their consent. If only one
party appeals for divorce, the divorce must proceed through mediation or court verdict, which
normally takes longer. 7

8Similar letters were also required for marriage.

9To see how small the number was by Western standards, the crude divorce rates for the US.
and the UK. were 4.70 and 2.96 per thousand in 1991 (United Nations, 1996). Even the rates
for Hong Kong and Taiwan, two neighboring Chinese communities, were also slightly higher. In
1991, the two regions recorded rates of 1.1 (Census and Statistics Department, 2002) and 1.38
(Directorate-General of Budget, 1997) respectively.

53

First, Chinese society has become more open and tolerant to divorcees, thanks to rapid
socioeconomic development and the spread of Western cultures. Second, divorce rules have
become more flexible recently (Palmer, 1995), especially since the implementation of the
new marriage registry regulation in October 2003. A major change in that regulation was
to simplify divorce procedures by revoking the requirement of certification from work units
and residence committees for getting both married and divorced. Finally, fast economic
growth since the end of 1970s has offered opportunities for individuals, especially women,
to become more educated and economically independent. There is some evidence that
well-educated women have a higher risk of divorce than poorly educated women (Zeng et
al., 2002), and that about 70 percent of all divorces are estimated to be initiated by wives

rather than husbands (Sheng, 2004).

3 Empirical Method

We are generally interested in the following divorce equation,

DIV, = .30 + 315150,: + 5211,: + Z flngz'j + _.3;,X,- + 62', (1)
j

where DIV,- is the divorce dummy, which equals 1 if a woman is divorced and 0 if she is
married. The variable S EC, is a binary indicator that equals 1 if the ith woman has given
birth two or more children.10 H2- is the ethnicity indicator that equals 1 for a Han woman,
and Cij stands for a birth cohort dummy that is equal to 1 if the woman was born in
the jth cohort. We also add a vector of covariates, Xiv to control for demographic and

geographic characteristics such as the education level, the rural dummy, and provincial

 

10We use the birth of a second child to measure fertility because our identification strategy
only applies to the second birth, which is permitted for ethnic minorities but not for Han women.
Moreover, higher-parity births above the second are not allowed, for both the Han and the
minorities, in most localities.

54

indicators. Equation (1) can be estimated by a linear probability or probit model.

The coefficient 1'31 is what interests us. The key hypothesis is that [31 < 0: that is,
having a second child has a. negative effect on marriage dissolution (or a positive effect on
marriage stability). However, the estimation of equation ( 1) may merely suggest a corre—
lation rather than a causal effect, because there could be a reverse causality running from
marriage stability to fertility, or they may both be affected by unobservable heterogeneity
in parental preferences. For example, couples who cherish family life more would have a
lower probability of divorce and a. stronger inclination to have more children. In this case,
the OLS estimate of (31 will be downward biased, thus implying that the stabilizing effect
of children on marriage will be overestimated. To correct such a bias, an IV technique can
be used and our task is to find a valid instrument that has no effect on divorce except
through the birth of a second child.

\Ve make use of China’s unique affirmative birth control policy to construct a new IV
that has not been used previously. To understand this strategy, note that the one-child
policy only applies to the Han. Chinese, which motivates us to use the Han women as the
treatment group and the ethnic minority women as the control group. However, a distinct
feature of the birth-control policy is that. the timing of the treatment is not discrete: that is,
there is no simple distinction between no treatment and treatment, as would be the ease in
most situations to which a DD method may be applied, such as joining a training program.
Rather, the treatment is a matter of degree that varies with the age of the woman. For
example, a Han woman who was 25 years old in 1979 was more affected by the one-child
policy than a Han woman who was already 35 years old, because on average the older
woman had fewer childbearing years left. Thus, we measure the treatment timing by a set
of dummy variables of (post-treatment) birth cohorts to capture the potential non-linear

55

degrees of treatment by age.

In practice, we specify the first stage of the 2SLS estimation as
SECZ' = (1'0 + (rlef + anjcij + :(r3jHl- * C2]; + (taxi +1.5, (2)
J J

and equation (1) becomes the second stage. Apart from the cohort dummies and the
interaction terms, all of the variables are as specified in equation ( 1). In (2), we omit all
dummies for the pre-treatment cohorts, which will be defined in Section 5.1. Essentially,
the pre—treatment group includes those cohorts of women whose second children were born
by the time that the one-child policy took effect. In this equation, Hi and Cij pick up the
two main effects of being Ham on fertility and of the treatment timing on fertility.

The key variables in (2) are the interactions of the policy timing (indexed by birth
cohort dummies) and the Han. dummy, which serve as the identifying instruments for
SEC, The coefficients on the interaction terms, or a3j, are virtually DD estimators.
Assuming that without the one-child policy the changes in the fertility of Han women
and minority women would have been the same between 1979 and 1990,11 the interactions
pick up the effects of the one-child policy on fertility for each cohort. In other words, the
interaction terms measure the fertility gap between the Han and the minority women that
is attributable to the affirmative one-child policy. We expect negative coefficients on. the
interaction terms, which will mean that the birth control policy has lowered the fertility
of the Han Chinese relative to the fertility of the ethnic minorities. These DD estimators
identify the exogenous variations in fertility that has been incurred by the one-child policy,
and they enable us to estimate the causal effect of fertility on marriage stability.

To avoid the potential finite-sample bias of 2SLS estimates brought by a large number

 

11This is the same as assuming that a3j is zero without the one-child policy.

56

of instruments,12 we also specify an alternative form of estimation that involves a much
smaller set of instruments. Rather than using the birth cohort dummies, we model the
treatment timing (Ti) as a quadratic function of the birth year, Ci, so that the equation

of interest and the first-stage relationship are given by

DIVZj = 30 + ,513EC, + JQHZ', + ,33Tz' + £321Xz‘ + 52' (3)

SEC/'1' = (.10 + 01Hi+ a‘QTZ' + 03112-1: Ti + OZXZ' + Uz', (4)

where T,- = 71C,- +726? +7319, +74PZ- * C,- + 75 P27 *sz; P,- is a dummy variable that equals
1 if a woman is born into the post-treatment group. Compared to the strategy that was
specified by equations (1) and (2), it is not. as straightforward to see the first-stage effect
of the one-child policy on fertility for each cohort from equation (3), but our empirical
analysis will show that our estimates are not sensitive to the function form that is used to

model cohorts.
4 Data

We mainly use the 1% sample of the 1990 Chinese Population Census that was collected
by the Chinese National Bureau of Statistics (formerly the State Statistical Bureau). This
was the fourth census of its kind, following these that were conducted in 1953, 1964 and
1982.13 We also use the 1982 census for graphical presentations, but do not report the

estimation results using it because they are qualitatively similar to those for the 1990

 

122SLS estimates can be biased in the. same direction as OLS estimates when many instruments
are used and the first-stage relationship is weak, even with very large datasets (Bound et al.,
1995 .

”The 1982 and 1990 censuses are the most appropriate for the application of the DD method.
The 1953 and 1964 censuses are too early for our purposes, because the one—child policy was
initiated in 1979. The latest census, or the fifth round, was conducted in 2000, and is too late for
the application of the DD method, as almost all of the women in the 2000 census who reported
fertility (the 1951-1985 cohorts) fall within the post-treatment period, as defined in Section 5.1.

57

census. The 1982 census is less appealing than the 1990 census because it does not have
a rural indicator, and more importantly the policy effect might be estimated less precisely
for some of the late cohorts because they were too young to have given birth by 1982.

The 1% sample of the 1990 census covers 2,832,103 households. The dataset contains
a record for each household, and includes variables that describe the location, type, and
composition of the households. Each household record is followed by records for all individ-
uals who reside in the household. Given the huge population size, the census only collects
basic information from each household and individual. Variables that relate to individu-
als include demographic characteristics, occupation, industry, education levels, ethnicity,
marital status, and fertility.

To facilitate our analysis, we restrict the sample to women aged 20—64 who were or had
been married by the census year.14 \Ne use 20 as the lower bound because it is the legal
age of marriage for women in China,15 and births to women below the age of 20 are rare.
We set 64 as the upper bound because the census did not ask women who were older than
this age for fertility information.

Table 2.1 gives the descriptive statistics for the full sample, and for four subsamples
defined by regions (rural vs. urban) and ethnicities (Han vs. minority). As seen in
Column 1, among the total of 2,772,823 women, 93 percent were Han and 79 percent had

rural residence. With regards marital status, 0.41 percent of the women were divorced.16

 

1“We drop women from the autonomous regions of Xinjiang and Tibet (1 percent) because these
two districts are highly dominated by minorities and observations of Han Chinese are very rare.
Moreover, Zeng and Wu (2000) show that the divorce rate for Xinjiang is remarkably higher than
other provinces in China (6 times the national average in 1990). They argue that this is partially
driven by less discrimination against divorcees in Islamic culture, to which belongs the Uygur,
the major ethnic group in Xinjiang. The exclusions do not qualitatively affect our conclusions.

15The Marriage Law of 1980 (amended in 2001) sets the minimum age of marriage at 20 for

Women and 22 for men.
16Among the married women, 4 percent were reported to be widows. Our results are not

Sensitive to dropping the widowed women.

58

The following columns indicate that the divorce rate is higher in urban areas (1.1 percent)
than in rural areas (0.23 percent), and higher for the minorities (0.63 percent) than for
the Han Chinese (0.39 percent). W hen we examine the divorce rate by family size, it can
be clearly seen that the rate decreases with more children. In the full sample, the risks of
divorce for childless women and for women with an only child are roughly 5 and 3.5 times
the risk for women with 2 or more children. This negative association between the divorce
rate and the number of children is consistent across all subsamples.

Several other aspects of the data in Table 2.1 are also worth noting. First, the average
number of children per woman is far greater than one (the first row), despite the fact that
the one-child policy had been in force for ten years by the time of the census in 1990.
Second, there are nontrivial fertility gaps both between rural and urban areas and between
the Han and the minorities, regardless of whether we measure fertility by the number of
children or by the proportion of women who had a first, second, or third child. The rural-
urban and Han-minority differences in the average number of children are 0.9 and -0.4
respectively. Finally, the figures regarding education level suggest that rural women had
inferior levels of education compared with urban women, and that the Han women were

better educated than the minorities on average.17

5 The Effect of the One-Child Policy on Fertility

In this section, we systematically test whether China’s birth control policy has had an
effect on fertility, and measure the magnitude of this effect if it is found. we first explore

the data and identify the pre-treatment birth cohorts. We then estimate equation (2) to

 

17'The census coded the education level into seven categories: Illiterate, Primary School, Junior
High School, Senior High School, Technical School, Junior College, and University. As the pro-
Portion of levels above senior high school is very small (2 percent), we group senior high school
and all higher levels as the top level.

59

examine the effect of the one—child policy on fertility, and finally discuss the validity of the
identification assumption of the DD method by performing sensitivity tests. For all of the
estimations, we employ OLS regressions because most of our analysis involves comparing

the means between groups, and the linear model is more convenient.18

5.1 The Pre-Treatment Group

To estimate equation (2) (or (4)), we need to identify the pre—treatment group, or the
group of women whose second child had been born by the implementation of the one-child
policy. This group includes those women who, by 1979, already had their second child if
they wanted and were able to do so. We resort to the 1982 and 1990 censuses to determine
the cutoff cohort for the pic—treatment group.

The solid curve in Figure 2.1 depicts the probability of having a second child by birth
cohort for the 1982 census. It shows that the probability of having a second child increases
slightly with birth year for the cohorts of 1926-1935. This increase in fertility probably
reflects better nutrition, health, and living conditions.19 The probability becomes almost
stable at the level of 96-97 percent for the 1935—1945 cohorts, which means that in 1982,
women in the age range of 37-47 had a roughly equal chance of having a second child.
According to studies in the literature of medicine and demography (Cheng et. al., 1992;
Tu et al., 2000; Liu et al., 2005), the primary infertility rate for Chinese couples, or the
proportion of couples who are not able to achieve pregnancy when they have been trying for
a certain time, was about 1.3-2 percent in the 1980s. Presumably, the secondary infertility
rate should be higher, which suggests that 96-97 percent is almost the biological limit

for the percentage of Chinese women who have a second child. Therefore, women in the

 

18Using the probit model generates very similar results (not shown).
19China was politically unstable and. involved in various wars between 1926 and 1949, which
may have affected fertility negatively.

60

1945 and earlier cohorts were almost unaffected by the one-child policy. In contrast, the
probability starts to drOp sharply for the 1946 and later cohorts, thus implying that they
could be affected by the one-child policy.

To check whether the probability of having a second child for the 1945 and earlier
cohorts actually did stabilize after 1982, we plot a dashed curve for the 1990 census in
Figure 2.1. If some of the women in these cohorts had a second child after 1982, then we
should be able to see this by comparing the 1982 and 1990 curves. Interestingly, the figure
confirms that the probability of having a second child for the 1950 and earlier cohorts
indeed stabilized after 1982. The two curves almost coincide with each other for the 1950
and earlier cohorts, which suggests that the probability of having a second child for these
cohorts did not change over the eight-year period. However, for cohorts later than 1950,
there is a shift to the right from 1982 to 1990, reflecting the age effect for young women
whose second births were more likely to be observed in 1990 as they became older.

In Figures 2.2 and 2.3, we re-plot the probability of a second birth for the Han and
minority subsamples, respectively. The probabilities for the 1990 census are also reported
in the first and second columns of Table 2.2 (the tables for the 1982 census are omitted
hereafter). In both figures, for the 1945 and earlier cohorts, the 1982 and 1990 curves more
or less coincide with each other and look similar to those in Figure 2.1. Again, for the
1935-1945 cohorts the probability for Han women reaches 96-97 percent, which is almost
the biological limit for second births. For the minorities in the 1935-1945 cohorts, the
probability is marginally lower but still quite stabilized.20 However, for the 1946 and later

cohorts, the drop in probability seems much steeper for the Han (Figure 2.2) than the

 

20Liu et al. (2005) find that the infertility rate for minorities is a little higher than that of the
Han.

61

minorities (Figure 2.3), whether we look at the 1982 curve or the right—shifted 1990 curve.
This suggests a large Han—minority fertility gap for the 1946 and later cohorts.

Putting these together, we find that 1945 is the cutoff cohort for stabilized probability
both across cohorts (1935-1945) and across ages (between 1982 and 1990), and that women
in the 1945 and earlier cohorts had a rate of second births approximating the biological
limit. As the earlier cohorts generally bore children earlier in their lifecycle than the later
cohorts, it is safe to assume that women in the 1945 and earlier cohorts (aged 34 or above
in 1979) had already had their second child if they wanted and were able to by the time
that the one-child policy came into force. Thus, we use the 1945 and earlier cohorts as the

pre—treatment group in our DD estimations."21

5.2 The DD Estimation

Given the cutoff cohort. for the treatment timing, we are now able to estimate the first-
stage relationship relating the one—child policy to the second-birth behavior. First, to see
more clearly how the difference between the Han. and the minorities in the probability of a
second birth evolves across cohorts, we sketch the differences by birth cohorts for the 1982
census in Figure 2.4. The differences oscillate around zero for the 1.945 and earlier cohorts,
and on the whole, the Han-minority difference for these cohorts is slightly negative and
marginally significant at the ten percent level (-0.2 percentage points with the t-ratio of
-1.77). In a sharp contrast, the gap quickly widens starting with the 1946 cohort, and the

average difference for the post-treatment group (the 1946 and later cohorts) amounts to

 

21Strictly speaking, we conclude that women who were 37 or older in 1982 had already had
their second children. As we do not have data from 1979, we can only use 37 as the cutoff age,
which means that the cutoff cohort should be 1942. However, the age effect may be negligible
because the probability of second births almost reached the biological limit. Also, our results are
unaffected by using earlier cohorts as the cutoff, and the DD estimates for the 1943-1945 cohorts
are statistically zero in that case. '

62

 

-6.9 percent (t-ratio of -32.5).

Although it is tempting to attribute the expanding Han—minority fertility gap to the
one-child policy, there is still the possibility that the Han. women tended to marry and
give birth later than the minority women, conditional on the birth cohort. Put differently,
the increasing differences by cohorts may reveal the age effects rather than the varying
treatment (cohort) effects. To check this, we add the curve of Han-minority differences for
the 1990 census in Figure 2.4 and report the numbers in column 3 of Table 2.2.22 If there is
a sizable difference in the age of birth between the Han and the minorities, then we should
see a smaller gap eight years later because, with the absence of the one-child policy, the
fertility of Han and minority women would approach a similar level as they aged (as for the
1945 and earlier cohorts). Nonetheless, as is evident in Figure 2.4, the downward shift of the
1990 curve relative to the 1982 curve shows a larger instead of a smaller fertility gap over
the eight-year span, as the average difference for the post-treatment cohorts rises to -9.1
percent (t—ratio of —63.57).23 That the Han-minority differences were enlarged when more
of the second birth behavior had been observed by 1990 adds to our confidence that the
one-child policy has been very effective in deterring the Han from having second children.

Another feature of Figure 2.4 is that the treatment effect is likely to vary across ages.
As shown in Table 2.2, for the post-treatment group, the Han-minority difference in the
probability of having a second child increases (in absolute value) with birth year and then
decreases monotonically. The gap roughly has a U-shape and reaches the maximum of 20

percentage points with the 1958 cohort. There are probably two reasons for this convex

 

22To save space, we do not report the differences for each pre-treatment cohort, as they have
little to do with the one-child policy.

23The parts of the pre-treatment group in the 1982 and 1990 curves are close to each other. The
average difference for the 1945 and earlier cohorts in the 1990 census is not statistically different
from zero (t-ratio of 1.46).

63

shape. For the earlier cohorts, some Han women had already had their second child by
1979, and hence were not subject to the one—child policy. For the later cohorts, although
the Han women were more likely to be affected by the policy, some minority women who
wanted to have a second child may not have done so by the census year (the youngest
women were 20 years old in 1990). Thus, the fertility gap appears to be of the greatest
magnitude in the cohorts near 1958, or those women who were about 21 years old in 1979
and 32 in 1990.

As the policy effect may change with the birth year in a nonlinear way, cohort indica-
tors (and their interactions) are used in equation (2) to capture the non-linear feature.24
The DD estimates (the estimated 03]) that measure the effect of the one-child policy for
each cohort are reported in the fourth column of Table 2.2.25 Column 4 is a simple DD
regression without any covariates (Xi), and the estimates are merely the results of sub-
tracting the Han-minority difference (column 3) for the pre—treatment group from that for
each post-treatment cohort. The coefficients on the interaction terms for the 1946-1970
cohorts are all negative and significant at the one percent level (except for the five percent
level for 1946-1947), and the F —test (255.8) strongly rejects the hypothesis that these co-
efficients are jointly zero. The magnitude of the effect first increases with the birth year,
peaks at 20.2 percent for the 1958 cohort, and descends thereafter. The average effect
for the post-treatment group is reported in the last two rows. On average, the one-child
policy has lowered a Han woman’s probability of having a second child by 9.2 percent-

age points, compared to the probability for a minority woman before and after the policy

 

2“ Equation (4), which includes a quadratic specification of birth cohort, is also estimated (results
not shown). Although the coefficients virtually measure the U-shape relationship observed, they
are not as transparent to interpret as those of equation (2). The table is available to interested
readers. ,

25’The coefficients on other variables, including the Han, cohort, education (columns 5 and 6),
rural, and provincial dummies (column 6), are not shown due to space limitations.

64

treatment. If we focus on the relatively early post-treatment cohorts (1946-1959), whose
second-birth behavior was more likely to have been fully observed, the policy effect. rises

to 11.6 percentage points.

5.3 Sensitivity Tests

Although the previous analysis found that the one-child policy has had a significant effect
on reducing the fertility of the Han Chinese relative to the minorities, we need to make
sure that it is not mainly picking up the effect of other policy shocks or economic changes,
which may be contained in the error term in equation ( 1). The key assumption of the DD
identification is that without the one-child policy, the changes in the probability of having
a second child for the Han and the minorities would have been the same between 1979 and
1990. If there are other policy shocks or changes in social-economic variables in the same
period that have affected the fertility behavior of the Han and the minorities differently,
then the DD method may have picked up the effect of these policies or changes. In case
these policies or changes are omitted in equation (1), the validity of our instruments would
be questionable. Although by design we do not know any of the unobservable shocks or
variables, we attempt to justify the DD identification in two ways, as demonstrated below.

5.3.1 DD Estimations with Control Variables

The first way to check the sensitivity of our DD estimates is to add demographic and
geographic controls to the DD regression, as we do in columns 5 and 6 of Table 2.2. In
particular, we use the education dummies to capture the opportunity cost of children and
the preference of women, and use the provincial and rural dummies to capture geographic

factors that may influence parental preferences and the costs of having children.26 Adding

 

26See Behrman and Wolfe (1984) and Rosenzweig and Schultz (1985) for the potential deter-
minants of fertility.

65

these variables not only controls for other policies or social-economic conditions that may
affect fertility, but also tests the robustness of our DD estimates. If the DD estimators
have picked up the effect of cross-cohort changes in other differences between the Han and
the minorities, then controlling for these variables will significantly affect the magnitude of
the estimates. However, if the one—child policy is uncorrelated with these variables, then
our DD estimates should undergo little change.

Interestingly, the DD estimates are not very sensitive to the inclusion of these variables.
Column 5 reports the DD estimates from the regressions that control for women’s education
level. Compared to column 4, the magnitudes of the DD estimates only decrease by a small
degree for most of the cohorts. When we also include the provincial and rural dummies in
column 6, the magnitudes of the DD estimates even increase slightly and are very close to
those in column 4. Overall, controlling for these covariates causes very small changes in
the DD estimates, which suggests that our method may to a large extent have picked up

the effect of the one-child policy on fertility.

5.3.2 DD Estimations for Alternative Dependent Variables

The second approach of robustness check is to examine whether other personal or household
decision variables, which may reflect parental preference and the opportunity cost of having
children but. are not likely to be affected by the one-child policy, have changed in different
ways for the Han and the minorities in the treatment period. If other policies or changes
of social-economic variables have altered the preference and costs of having children of
the Han Chinese more than the minorities for the post—treatment cohorts, then the DD
estimators should pick up these effects when using these alternative decision variables as

dependent variables in equation (2). To validate our DD-based instruments, we expect

66

that the DD estimates for these variables will not be very large. If the estimates are large,
especially for the earlier post-treatment cohorts, then they will probably be picking up
other effects. In general. the census-provides very few variables. We will use all that are
relevant, including marriage, first-birth behavior, education, migration, and a few labor
market outcomes.

First we re-estimate equation (2) using the dummies for getting married and having a
first child as dependent variables. To a large extent, getting married and having a first.
child should not have been directly affected by the one-child policy, at least for the birth
cohorts in which the women had already been married or had their first child by the time
the policy came into force. For the very late cohorts, there may be a feedback (age) effect,
in that those who knew that they cou1d not have a second child may have chosen to marry
late or have their first child late. This feedback effect means that even without other policy
shocks or changes in social-economic variables, there may still be DD effects for marriage
and the first birth. Given this potential feedback effect that tends to increase the estimates,
if our estimates of these alternative dependent variables are still small, then we should be
confident that our DD estimators are not picking up the effect of other policy shocks or
changes in social-economic variables.

The DD estimates for the two new dependent variables, which are reported in the
first and second columns of Table 2.3, suggest that our previous estimates for the second-

27 In both columns, the

birth behavior should not be mainly driven by other factors.
coefficients are almost statistically zero for all but the very late cohorts, which could

reflect the potential feedback effect mentioned above. The average effects over 1946-1970

 

27As all women in the sample were or had been married, we expand it to all women aged
between 20 and 64, including those who never married, for the marriage equation.

67

are positive (09 percent for being married and 1 percent for having a first child), whereas
the average effects for the earlier cohorts (1946-1959) are not statistically different from
zero.

The same implications can be drawn from Figures 2.5 and 2.6, which plot the differences
between the Han and the minorities in marrying and having a first child, for both the 1982
and 1990 censuses. Note that the two curves in Figure 2.5 look almost the same, except
that the 1990 curve is a shift of the 1982 curve to the right by about 10 years. This
suggests that unlike in Figure 2.4, the gap for very late cohorts is very likely to be the age
effect that is removed in the 1990 census as more of the marriage behavior was observed.
Figure 2.6 exhibits the same pattern. except that the shift is approximately 8 years. Both
graphs show that for most of the cohorts (1946-1959) for which a large effect of the one-
child policy on a second birth has been identified, there is almost no cross-cohort change
in the Han-minority gap of the probability of marrying or having a first child. Thus, our
DD estimators for having a second child are unlikely to pick up the effect of other shocks
that have changed the preference and child costs, otherwise the marriage and first-birth
behavior should have been affected in a similar way.

The third and fourth columns of Table 2.3 present the DD estimates for two education
variables, the education level (1 to 7) and a dummy variable that indicates whether a
woman had graduated from or enrolled in school (versus dropped out of school). The
solid curve in Figure 2.7 depicts the differences between the Han and the minorities in
the probability of having graduated or enrolled for the 1990 census.28 Consistent with

the rising trend of the Han—minority difference in the graph, the DD estimates suggest

 

28The outcome variables illustrated in Figure 2.7 are not available in the 1982 census, so there
are no 1982 curves for comparison.

68

a significantly positive effect on women's education for all of the post-treatment cohorts.
The average DD effects on graduated/enrolled are 8.1 and 5.9 percent for the 1946-1970
and 1946-1959 cohorts respectively: This could be caused by a similar feedback effect
whereby the Han women who married late and gave birth late (because they could not
have a second child) may have stayed in school longer to receive a better education, or it
may reflect the unbalanced distribution of education resources between the Han and the
minorities during the treatment period. Although the true source of the DD effects on
education is unknown, it is not of great concern for our purposes because we have shown
that controlling for education in the fertility equation does not significantly change the DD
estimates.

Finally, we try the dependent variables of migration and several labor market outcomes,
which may to some extent capture the effect of the preference or child costs as well. We
report their DD estimates in Table 2.4 and sketch their Han-minority differences in Figure
2.7. Specifically, the four dummy variables measure whether a woman had migrated to
her current residence within the five years before 1990 (migrated), whether she was in
the labor force (working),29 whether her occupation belonged to the category of skilled
professionals (skilled), and whether she had lost the ability to work (unable to work). All
of the regressions control for education and geographical indicators.

As in Table 2.4, the DD estimates for these variables are either statistically insignificant
or small in magnitude, which suggests that at most a very small part, if any, of the DD
effect on a second birth comes from shocks or economic changes other than the one-child

policy. There appears to be little DD effect on the probability of migration (column 1),

 

29We use the urban subsample for the working regression because by the end of 19808 most
rural women worked for their own households (in either farm work or household work), and their
labor force participation rate was almost 100 percent in our sample.

69

except for some very late cohorts for which the magnitudes are merely around 1 percent.
In column 2, hardly any DD effect can be detected in the estimation for working, as the
coefficients are both close to zero and statistically insignificant. Although the estimates
for skilled (column 3) and unable to work (column 4) seem to be statistically different from
zero across most cohorts, the size of the DD effects is rather small, with the maximum
magnitudes among the 1946—1970 cohorts reaching only 2 percent for the former and 1
percent for the latter. Figure 2.7 also shows that the Han-minority differences in the four
variables do not change dramatically between the pre— and post-treatment periods, as their

curves all remain approxin'iately horizontal.

6 The Effect of Fertility on Divorce

Having established a robust first-stage relationship l)etween fertility and the birth-control
policy, now we run OLS and QSLS regressions to test whether having a second child has
an effect on reducing the probability of divorce in China, using the DD estimators to
instrument fertility. We also check the heterogeneity of the effect by performing the same
estimations for various subsamples.

The estimates of the effect of having a second child on divorce risk are presented in
Table 2.5. In particular, we report the OLS estimates of equation (1) and two sets of
2SLS estimates of equations (1)-(2) and equations (3)-(4). To save space, we only report
the coefficients on fertility.30 The first three columns show the results without covariates
Xi, and the next three columns show the results with eovariates. The top panel shows
the results for the full sample, the middle panel shows the results for rural and urban

subsamples, and the bottom panel shows the result for subsamples by education level.

 

30The OLS estimates of 61 in equation (3) are omitted here because they are very similar to
those in equation (1) in both their magnitudes and t-statisties.

70

Fertility and divorce are negatively correlated in the full sample. The OLS estimate
in column 1 suggests that the presence of a second child reduces the probability of being
divorced by 0.95 percentage points, which is more than twice the sample average. However,
this is partly due to uncontrolled demographic and geographic factors, because the OLS
estimate with controls reduces to 0.71 percentage points (column 4). When we use the DD
estimators as instruments for having a second child, the 2SLS estimates with or without
covariates both remain significant at the one percent level, which suggests a causal effect
of a second birth on the likelihood of being divorced. Interestingly, the 2SLS estimates are
smaller (in absolute value) than the corresponding OLS estimates, which is consistent with
our priors that the fertility coefficients are likely to be overestimated (biased downwards)
due to simultaneity or omitted family preferences. It is also noteworthy that the 2SLS
estimates that use two different. sets of instruments are quite similar in fact.

To ascertain whether the effect of children on divorce risk varies with residence area or
education level, next we stratify the sample into rural/ urban and four education subsam-
ples. As shown by the OLS estimates in columns 1 and 4, the negative correlation between
the second childbearing and the probability of being divorced is consistently existent across
various subsamples, but the ZSLS estimates are somewhat mixed in signs.31 The 2SLS es-
timates for rural women are still significantly negative, but those for urban women turn
positive and not statistically different from zero. Among the four education subsamples,
the only causal effect of childbearing appears to be an increase in the likelihood of being

divorced for the least educated (illiterate) women. Although the 2SLS estimates for better

 

31To be concise, we do not report the first-stage estimates for these subsamples. In general,
the first-stage effect of the one—child policy on the probability of having a second child is larger
in urban areas and for more educated women. The numerical estimates for these subsamples are
reported and analyzed in our earlier study (Li et al., 2005).

71

educated women suggest a stabilizing effect of children on marriage, most of them are
imprecise. Despite the mixed signs, the 2SLS coefficients are less negative than (or of the
opposite sign of) the OLS coefficients across all subsamples, which again confirms that the
OLS estimates are downward biased.

Finally, we divide the sample by the interaction of rural/ urban and education level,
and report the regression results in Table 2.6. The upper panel shows the estimates for
the rural subsamples (by education) and the lower panel for the urban subsamples (by
education).32 Not surprisingly, the OLS estimates continue to show a significantly negative
correlation between a second child and the probability of divorce, and the relationship is
more pronounced in urban than in rural areas, regardless of education level. Compared
to the OLS estimates, the 2SLS estimates for the rural subsamples are less negative but
statistically insignificant, except for a significantly positive effect that is identified for the
group of illiterate women. Across the urban subsamples, all of the 2SLS estimates exhibit
a positive sign, but are statistically insignificant. Overall, the OLS estimates of the fertility
effect are consistently downward biased, because a second birth has little effect on reducing
the probability of being divorced for most groups as long as the endogeneity of fertility is

accounted for.

7 Conclusions

In this paper, we explore the causal link between fertility and marriage stability in China,
making use of a unique birth control policy to break the endogeneity of fertility. China’s

affirmative one-child policy allows us to conduct a natural experiment, which enables us to

 

32Again, the first-stage results are not reported. As women with senior high school education
or above are rare in the rural subsample, they are reclassified into the group of junior high school
and above. The first-stage results suggest that. education plays a bigger role in changing the
treatment effect of the one-child policy in rural areas than in urban areas (Li et al., 2005).

72

identify the effect of fertility on marriage stability by introducing the exogenous variation
in fertility that results from the enactment of the policy. Such a natural experiment is a
rare opportunity, whether for the analysis of the effect of fertility on marriage stability or
for economics in general.

Employing an extract from the 1982 and 1990 Chinese Population Censuses, we first
identify a strong first-stage relationship in which the one-child policy has been effective in
reducing the probability of second births among the Han Chinese compared to the eth-
nic minorities. This relationship is robust to the control for demographic and geographic
variables and two sensitivity tests. Using the DD estimators of the policy effect as instru-
ments for fertility, we then find that the negative correlation between a second birth and
the probability of being divorced is much attenuated. In other words, after we address
the endogeneity problem, the second childbearing appears to have little causal effect. on
stabilizing marriage.

Ever since its inception in the late: 1970s, China’s one-child policy has been controversial,
and has drawn attention from politicians, the mass media, and academics. Even if we
ignore the other positive and negative aspects of forced birth control policies, the one-child
policy still has a mixed effect. on economic development. On the one hand, as shown by Li
and Zhang (2007), the resultant population reduction has helped the growth of the Chinese
economy since the late 1970s. On the other hand. the policy may have changed many other
aspects of the family dramatically. While some researchers (e.g., W’ang. 2001) attribute
part of the fast rising divorce rate in China to demographic changes such as declining

fertility, our findings suggest. that the, role of the one-child policy is minimal.

73

Figure 2.1: Probability of Having a Second Child by Cohorts
Whole Sample for 1982 and 1990 Censuses

F"

are /

(D...

 

ffi—i
(Q4
JO...
fl:—
(0...
N-

v-__l

 

 

o—

 

l i 1 l T T 1 i 1 i i T
1915 1920 1925 1930 1935 1940 1945 1950 1955 1960 1965 1970
BirthCohort

f i 1982 ----- "1990

 

 

 

74

Figure 2.2: Probability of Having a Second Child by Cohorts
Han Sample for 1982 and 1990 Censuses

F"

02- /

w...

 

[\‘q
(0....
.lD._i
#2..
Q-

(V...

 

Pd

0‘

 

 

I I l I I I j I I I F

I
1915 1920 1925 1930 1935 1940 1945 1950 1955 1960 1965 1970
BirthCohort

 

 

Han 1982 ------ Han 1990

 

 

 

Figure 2.3: Probability of Having a Second Child by Cohorts
Minority Sample for 1982 and 1990 Censuses

 

 

 

 

 

 

 

a? , ”fr _, a;
09 s
[\- —l
(D- ..
m. _
s, _
(V). .1
(\g o
. I I I l I j I I I I . r
1915 1920 1925 1930 1935 1940 1945 1950 1955 1960 1965 1970
Birth Cohort
Minority 1982 --—--- Minority 1990]

75

Figure 2.4: Probability of Having a Second Child by Cohorts

Han-Minority Differences for 1982 and 1990 Censuses

l

l

l

J

l

l

l

1

l

1

 

-.35 -.3 -.25 -.2 -.15'-.1 -.05 o .05 .1

 

 

I I I I I I I I I I I I
1915 1920 1925 1930 1935 1940 1945 1950 1955 1960 1965 1970

l l l l J l l l L

l

 

-.35 -.3 -.25 -.2 -.15'-.1 -.05 o .05 .1

Birth Cohort

 

 

1982 ----- - 1990

 

 

Figure 2.5: Probability of Being Married by Cohorts
Han-Minority Differences for 1982 and 1990 Censuses

 

 

 

 

 

I I I I I I I I I I If I
1915 1920 1925 1930 1935 1940 1945 1950 1955 1960 1965 1970
Birth Cohort

1982 ------ 1990

 

 

 

76

Figure 2.6: Probability of Having a First Child by Cohorts
Han-Minority Differences for 1982 and 1990 Censuses

1
l #L

1

J

 

L

l

l

L

 

-.35 -.3 -.25 -.2 -.15°-.1 -.05 o .05 .
l

l

 

I I I I T I I I I I T I
1915 1920 1925 1930 1935 1940 1945 1950 1955 1960 1965 1970
Birth Cohort

 

—-—— 1982 ------ 1990

 

 

Figure 2.7: Probability of Other Outcomes by Cohorts
Han-Minority Differences for the 1990 Census

 

. . I ..
. __ Hora-«$139!, gunk. _.. I. .
‘ . . . ___\. lir- ) .‘i fi. ‘5- flag“ . > ‘fi

,. 1'
0.. '.,-_ .‘.. '__,‘.~.’-i-v ,-
. o —i ‘L—a—udu-L-fil‘-fi,‘a'
- h .. .
‘ "-.' \. .5 - - I

. ,__ e .-. a A.
m—t'“‘sWVr-W—9wfltr~"’fiz—i - -
0”"2" “'13- ‘35

      
 

N —1
I-

 

('34
I.

 

I I I I I I I l I I
1925 1930 1935 1940 1945 1950 1955 1960 1965 1970
Birth Cohort

 

 

Graduated/enrolled ------- Migrated
--+-—- Working ._-o...;,-..._ Skilled
~-~---<‘+-- w Unable to work

 

 

 

77

Table 2.]: Descriptive Statistics for the 1990 Census: Ever-Married Women Aged 20-64

Mean and (standard deviation)

 

 

 

Full sample Rural Urban Han Minority
Variable (l) (2) (3) (4) (5)

. 2.72 2.90 2.04 2.70 3.13
0‘1““ ever born (1.94) (1.98) (1.60) (1.91) (2.20)
21 child (=1 if mother had 0.939 0.940 0.935 0.939 0.933
any child) (0.240) (0.238) (0.247) (0.239) (0.250)
22 children (=1 if mother 0.693 0.748 0.484 0.689 0.753
had more than 1 child) (0.461) (0.434) (0.500) (0.463) (0.431)
23 children (=1 if mother 0.451 0.491 0.294 0.445 0.527
had more than 2 children) (0.498) (0.500) (0.456) (0.497) (0.499)
A c 38.3 38.0 39.4 38.3 37.8

g (11.9) (12.0) (11.3) (11.9) (12.1)
Han 0.935 0.929 0.959 _ _
(0.247) (0.257) (0.197)
Rural 0.794 _ _ 0.788 0.871
(0.405) (0.409) (0.335)
Divorced (all women) 0.0041 0.0023 0.0110 0.0039 0.0063
(0.0636) (0.0474) (0.1044) (0.0624) (0.0792)
Divorced (no child) 0.0107 0.0078 0.0210 0.0099 0.021 1
(0.1030) (0.0881) (0.1432) (0.0991) (0.1437)
Divorced (1 child) 0.0076 0.0041 0.0135 0.0074 0.0123
(0.0870) (0.0636) (0.1154) (0.0857) (0.1 104)
. . 0.0022 0.0013 0.0074 0.0021 0.0036
D‘Vorced (32 Ch‘ld’e“) (0.0469) (0.0366) (0.0855) (0.0458) (0.0596)
“literate 0.318 0.372 0.112 0.310 0.442
(0.466) __ (0.483) (0.315) (0.462) (0.497)
Prim school 0.361 0.403 0.197 0.363 0.323
'7 (0.480) (0.491) (0.398) (0.481) (0.468)
J . r hgh ch 1 0.223 0.189 0.354 0.227 0.164
“m0 ‘ 5 0° (0.416) (0.391) (0.478) (0.419) (0.370)
Senior high school or 0.098 0.036 0.337 0.100 0.071
above (0.297) (0.186) (0.473) (0.300) (0.256)
Number of observations 2,772,823 2,200,468 572,355 2,592,489 180,334

 

Notes: The samples include women aged 20-64 who were or had been married by the time of the census,
excluding those in Xinjiang and Tibet Provinces. The data are from the l-percent 1990 Chinese

Population Census.

78

Table 2.2: Differences-in-Differences Estimates of the Effect of the One-Child Policy
on the Probability of Having a Second Child: 1990 Census

 

Dependent variable: probability of having a second child

 

DD estimates

 

 

 

. Han -Minority . Education
Han Mlnor differences No covariates Education as and area as
covanate coVariates
Birth cohort (l) (2) (3) (4) (5) (6)
Pre-treatment
(N = 819,762)
1926 - 1945 0.954 0.953 0.001 - - -
Post-treatment
(N= 1,953,061)
1946 0.954 0.967 -0.013*** -0.015** —0.003 -0.012*
1947 0.945 0.959 —0.014*** -0.015** -0.006** -0.013**
1948 0.931 0.953 0023*" 0024*" 0019*" 0028*"
1949 0.910 0.947 0036*" 0038*" 0030*" 0040*"
1950 0.882 0.938 -0.056*** -0.058*** -0.052*** 0058*"
1951 0.853 0.925 0072*" 0073*" -0.070*** 0080*“
1952 0.824 0.916 -0.091"”"* 0093"" 0088*" 0099*"
1953 0.780 0.896 0116*" -0.118*** 0110*" -0.124***
1954 0.740 0.885 0144*" 0146*" -0.136*** 0146*"
1955 0.712 0.877 -0.164*** 0166*" 0155*" -0.l67***
1956 0.681 0.852 0171"" 0172*" 0165*" 0177*"
1957 0.653 0.850 0197*" 0199“" 0184*" 0196*"
1958 0.619 0.819 0201*“ 0202*" 0186*" 0199*"
1959 0.582 0.780 0198*" -0.199*** 0179*" 0198*"
1960 0.539 0.721 0182*" 0183*” 0161*" -0.181***
1961 0.544 0.704 0160*" 0161*" 0138*" 0158*"
1962 0.511 0.661 0150*" -0.151*** 0130*" 0151*"
1963 0.437 0.587 -0.150*** 0151*" 0129*" 0152*"
1964 0.373 0.516 0143*" 0144*" 0117*" 0140*”
1965 0.306 0.438 -0.132*** 0134*" —0.110**"' -0.137***
1966 0.238 0.355 -0.1 17*" 0119*" 0095*" 0124*"
1967 0.171 0.267 -0.096*** -0.097*** -0.072*** -0.106"""*
1968 0.112 0.184 -0.072"‘** -0.074**"' 0050*" 0087*"
1969 0.075 0.133 —0.058*** -0.060*** 0034*" -0.073***
1970 0.044 0.073 0028*" 0029*” -0.005 0045""
1946 - 1970 0.578 0.669 -0.091*** -0.092*"'* -0.071*** 0080*"
1946 - 1959 0.779 0.893 —0.1 14*“ -0.116*** 0106*" -0.116"‘**

 

Notes: *, **, and *** represent significance levels of 10, 5, and 1 percent. Column 5 controls for
women’s education (dummies indicating levels of illiterate, primary school, junior high school, senior
high school, technical school, junior college or university), and column 6 controls for provincial and
rural indicators in addition to education. N represents the number of observations.

79

Table 2.3: Differences-in-Differences Estimates of the Effect of One-Child Policy on
Other Fertility and Education Outcomes: 1990 Census

 

Dependent variable

 

 

 

 

All women Ever—married women

Being married Having a first child Education level Graduated/enrolled
Bifih (1) (2) (3) (4)
cohort
Mean
(s.d.) of 0.891 (0.311) 0.939 (0.240) 2.143 (1.077) 0.551 (0.497)
dep. var.
DD estimates
1946 0.001 (0.28) -0.003 (-0.66) 0116*" (7.60) 0073*” (9.50)
1947 0.001 (0.27) 0.001 (0.34) 0102“" (6.93) 0065*" (8.60)
1948 0002 (-0.57) :0.001 (0.27) 0115*" (7.92) 0069*" (9.37)
1949 -0.001 (-0.38) 0.001 (0.43) 0099*" (7.38) 0047*“ (6.95)
1950 -0.001 (-0.33) 0.003 (0.77) 0093*" (6.91) 0068*" (9.89)
1951 0.001 (0.28) —0.002 (-0.56) 0083*" (5.88) 0052*“ (7.27)
1952 —0.002 (-0.68) 0.002 (0.61) 0085*" (6.77) 0056*“ (8.72)
1953 -0.003 (090) 0.001 (0.39) 0124*" (9.68) 0063““ (9.73)
1954 -0.000 (013) -0.001 (-0.l7) 0094*“ (7.70) 0052“" (8.43)
1955 -0.001 (021) 0.000 (0.07) 0109*" (8.87) 0062*“ (10.02)
1956 -0.001 (-0.44) 0.002 (0.73) 0083*" (6.67) 0050*“ (7.96)
1957 -0.000 (-0.12) 0.001 (0.47) 0125"" (10.38) 0069*" (11.30)
1958 0.000 (0.14) -0.001 (-0.20) 0126*" (10.08) 0054*" (8.56)
1959 -0.000 (-0.02) -0.003 (-0.90) 0149"" (10.45) 0066*" (9.11)
1960 0.002 (0.43) 0.001 (0.22) 0162*" (11.84) 0064*“ (9.27)
1961 0.002 (0.48) 0.007“ (1.93) 0174*" (11.59) 0080*" (10.48)
1962 0.005“ (1.72) 0.003 (1.06) 0190“" (17.48) 0086*” (15.61)
1963 0.006" (2.42) 0.000 (0.16) 0204*" (20.29) 0091*“ (17.86)
1964 0011*” (4.24) -0.005* (-1.81) 0242*" (23.17) 0110*" (20.87)
1965 0008*" (3.04) -0.017"”'”" (-6.21) 0241*" (22.66) 0119*" (22.12)
1966 0.004 (1.61) 0025*" (-8.90) 0258*" (23.83) 0123“" (22.40)
1967 0019*" (-6.71) 0042*" (-l3.45) 0288*” (23.79) 0154*" (25.08)
1968 0053*" (-21.13) 0044*" (-14.37) 0.283‘" (23.62) 0.158‘" (25.91)
1969 0086"" (-33.07) 0067*“ (—18.27) 0321*" (22.50) 0187*" (25.84)
1970 0092*" (-35.69) 0048*" (-10.51) 0328*" (18.65) 0198*“ (22.10)
1946-70 0009*" (5.81) 0010*" (8.15) 0156*" (34.06) 0081*" (35.46)
1946-59 0001 (-0.65) 0.000 (0.36) 0105*“ (20.73) 0059*" (23.27)
Obs. 3,1 10,601 2,772,823 2,772,823 2,772,823

 

Notes: The t-ratios are shown in parentheses. ‘, ", and *** represent significance levels of 10, 5, and 1
percent. The ever-married-women sample (as used in this paper) refers to women aged 20-64 who were
or had been married by the time of the census. The all-women sample expands to all women aged 20-64,
regardless of their marital status. All regressions include rural and provincial dummies, and columns 1
and 2 include education as well.

80

Table 2.4: Difl‘erences-in-Differences Estimates of the Effect of One-Child Policy on

Migration and Labor Market Outcomes: 1990 Census

 

Dependent variable

 

 

 

Mi grated Working Skilled Unable to work
Birth (1) (2) (3) (4)
cohort
Mean
(s.d.) of 0.031 (0.175) 0.826 (0.379) 0.064 (0.245) 0.008 (0.090)
dep. var.
DD estimates
1946 0.002 (0.73) 0.009 (0.51) -0.002 (-0.48) 0009*" (5.24)
1947 0.003 (1.09) -0.018 (-l.14) -0.000 (-0.05) 0.007‘" (4.64)
1948 0.004 ( 1.44) -0.007 (-0.47) -0.006"‘ (-1.70) 0007*" (4.23)
1949 0005* (1.65) -0.002 (-0.18) —0.004 (-1.34) 0007*" (4.54)
1950 -0.000 (-0.01) 0.023 (1.61) -0.005 (-1.53) 0006*" (4.24)
1951 -0.000 (-0.06) —0.010 (-0.69) 0012*" (-3.63) 0007*” (4.44)
1952 -0.002 (-0.68) —0.010 (-0.79) -0.008*** (-2.73) 0006*" (4.59)
1953 -0.001 (-0.27) -0.000 (-0.03) 0009*" (-2.96) 0006*“ (4.63)
1954 -0.002 (-0.64) -0.019 (-1.58) 0012*" (-4.24) 0008*" (6.08)
1955 -0.002 (-O.96) -0.003 (-0.22) 0009*" (-3.03) 0007*” (5.31)
1956 0.001 (0.20) -0.03l*** (-2.56) 0014*" (-4.64) 0007*" (5.12)
1957 -0.002 (-0.83) -0.018 (-1.49) 0018*" (~6.08) 0008*" (5.83)
1958 -0.003 (-l.28) ’-0.008 (-0.63) —0.018"‘** (—6.05) 0007*" (5.28)
1959 -0.005 (-1.57) -0.016 (-1.19) -0.019**"' (-5.55) 0008*" (5.15)
1960 -0.010*" (-3.67) -0.001 (-0.10) -0.019**"' (-5.68) 0006*“ (4.15)
1961 -0.010*** (-3.17) -0.021 (-1.46) 0016*" (-4.49) 0007*" (4.28)
1962 0006*" (-2.60) -0.006 {-0.53) -0.018*** (-7.05) 0007*“ (6.13)
1963 -0.011*** (-5.09) -0.029*" (-2.95) -0.020*** (-8.05) 0008*" (7.17)
1964 -0.009"* (-4.19) -0.012 (-1.05) 0015*" (—6.00) 0008*" (7.23)
1965 —0.014*** (-6.41) 0.023" (1.96) 0020*" (-7.61) 0007*" (6.51)
1966 0009*" (—3.84) 0026" (-1.99) -0.015"‘** (-5.66) 0008*" (6.68)
1967 -0.016"‘*"‘ (-6.53) 0.003 (0.18) -0.017"'*"‘ (-5.74) 0008*" (5.94)
1968 -0.013*** (-5.42) -0.020 (-1.19) 0016*" (-5.60) 0008*" (6.05)
1969 -0.004 (-1.37) -0.002 (.010) -0.018*** (-5.17) 0008*" (5.22)
1970 —0.002 (-0.57) —0.022 (-0.61) —0.016*** (-3.95) 0010*" (5.05)
1946-70 0009*" (-10.04) -0.007 (-1.27) -0.012"“'"" (-10.58) 0007*" (15.38)
1946-59 0000 (-0.37) -0.009 (-1.63) -0.010*"‘* (-7.61) 0007*" (13.04)
Obs. 2,772,823 508,934 2,234,715 2,772,823

 

Notes: The t-ratios are shown in parentheses. ", ", and **"‘ represent significance levels of 10, 5, and 1
percent. Column 2 uses the sample of urban women, and column 3 excludes women who were not
working. All regressions include education, rural, and provincial dummies.

81

Table 2.5: OLS and 2SLS Estimates of the Effect of Having a Second Child on
Divorce: 1990 Census

 

Dependent Variable: Probability of being divorced

 

No covariates

With covariates

 

 

 

 

 

OLS 2$LS zsLs OLS 2SLS ZSLS
Sample (1) (2) (3) (4) (5) (6)
Instruments Han X Han >< Han 8 Han X
for having a - Cohort Cohort - Cohort Cohort
second child dummies quadratic dummies quadratic
fouggffiple 0.0095m -0.0076*** 0.0077*** -0.0071*** -0.0062*"'* -0.0067**"‘
{2' 772 823} (-9235) (-354) (0.53) (-62.53) (-2.85) (-311)
By arm
Rural *#* *## *# *** ** **
[0.0023] 0.0055 0.0062 0.0054 0.0056 0.0052 -0.0048
{2 200 468} (-57.86) (-2.67) (-230) (-56.71) (-224) (-204)
1333110] ~0.0116*** 0.0070 0.0057 -0.0116**" 0.0092 0.0081
{ 572,355} (-27. 59) (0.96) (0.75) (-26.44) (1.23) (1.03)
By education
:3‘3323‘4‘; 0.0093*** 0.0345*** 0.0213*" 0.009411" 0.02431'" 0.0137"
{8'83 039} (-46.05) (5.29) (3.24) (46.09) (3.98) (2.19)
1:333ng -0.0055*** 0.0012 0.0001 -0.0051*** 0.0037 0.0025
' - _ 7 - _ ..
{999,925} ( 36-47) (0.25) (41.0-) ( 32.60) (0.84) ( 0.56)
ggfiggl'gh -0.0099*** 0.0071 0.0041 0.007111" 0.0053 0.001 1
{618,315} (41.74) (-1.06) - (0.62) (-27.06) (-0.67) (0.14)
338342” 0.01 12*" 0.0034 0.0010 0.010211" 0.0009 0.0036
{2'71 544} (-2407) (—0.38) (0.10) (-1901) (0.09) (0.33)

 

Notes: Means of the dependent variable are shown in brackets, the sample sizes are shown in braces, and
the t-ratios are shown in parentheses. ‘, **, and *" represent significance levels of 10, 5, and 1 percent.
Columns 2 and 5 report estimates of the coefficient of having a second child on divorce in equations (1)
and (2) in the text. Columns 3 and 6 report estimates of the coefficient of having a second child on
divorce in equations (3) and (4) in the text. Other covariates include education, rural, and provincial

dummies.

82

Table 2.6: OLS and 2SLS Estimates of the Effect of Having a Second Child on

Divorce: 1990 Census (Rural vs. Urban)

 

Dependent Variable: Probability of being divorced

 

No covariates

With covariates

 

 

 

 

OLS zsLsg zsLs OLS 2SLS ZSLS
Sample (1) (2) (3) (4) (5) (6)
Instruments Han X Han X Han X Han X
for having a - Cohort Cohort - Cohort Cohort
second child dummies quadratic dummies quadratic
Rural sample
3010:2313 -0.0088*** 0.0346*** 0.0207*** -0.0089*** 0.0269*** 0.0158"
{819,060} (44.20) (5.44) (3.15) (44.69) (4.48) (2.51)
Primary
school -0.0038*** 0.0032 0.0010 -0.0040*** 0.0031 0.0014
[0.0019] (-28.19) (0.68) (0.22) (-28.51) (0.71) (0.33)
{887,177}

Junior high

222:? °' -0.0053*** 0.0028 0.0045 0.0055W 0.0062 0.0026

[0.0031] (-27.78) (0.35) ._ (0.56) (-27.20) (0.71) (0.29)

{494,231}

Urban

sample

131065;; 0.0141*** 0.0335 0.0122 0.0142*** 0.0385 0.0162
. _ S _

{63,979} ( 11.81) (1.4-) (0.47) ( 11.79) (1.52) (0.57)

3&3] 0.0125*** 0.0011 0.0037 0.0125*** 0.0024 0.0070

{112,748} (—14.50) (0.08) (0.25) (-14.30) (0.16) (0.45)

{338521911 0.01 10*" 0.0072 0.0056 0.0114*** 0.0099 0.0086

{202,785} (04.93) (0.51) (0.39) (-1491) (0.67) (0.56)

[831341310 0.0122*** 0.0109 0.0122 -0.0126*** 0.0110 0.0122

{192,843} (-1493) (0.92) (0.93) (-1510) (0.93) (0.92)

 

Notes: Means of the dependent variable are shown in brackets, the sample sizes are shown in braces, and
the t-ratios are shown in parentheses. *, *"', and *** represent significance levels of 10, 5, and 1 percent.
Columns 2 and 5 report estimates of the coefficient of having a second child on divorce in equations ( 1)
and (2) in the text. Colurrms 3 and 6 report estimates of the coefficient of having a second child on

divorce in equations (3) and (4) in the text. Other covariates include provincial dummies.

83

Appendix

I. Variation in Fertility (Second Births) across Years

The main analysis has tested the effects of the one-child policy by exploring
how the lien-Minority difference in fertility (probability of having a second child)
varies by the cohort of mothers. The fertility behavior we have researched only
reveals whether a woman had ever given a second birth (which is directly observed
in the census data) but not. when the birth was given. As the one-child policy was
introduced in 1979, it would also be interesting to see how fertility changed over
years, especially the years around 1979. Thus the purpose of this appendix is to
graphically show some results of the variation in fertility by year.

To obtain the data on birth timing, we need to link the information on the
birth year of children to their mothers. To do this, we use a subsample of the
women in the main analysis. First, we restrict the sample to women who are
labeled “household head” or “spouse of the head” because only in such cases can
their children be identified. Second, since only children living within the house-hold
can be identified, we restrict the mother’s age between 20 and 35 (the upper bound
is 40 for the 1990 census to allow for observations of women who were aged 25-29
prior to 1979) to make it. fairly certain that no adult children have moved out of
the household. Third, we drop women with no children as the fertility here is
defined as the probability of giving a second birth conditional on the completion of
the first birth. Finally, we use women’s fertility records to check whether the

family size (counting of children) is complete. About 1% of the 1.982 sample and

84

5% of the 1990 sample are drOpped due to discrepancy between the number of
children and mother’s reported fertility.

Table 2.7 reports the summary statistics for the two census samples
respectively. Using the 1982 sample, Figure 2.8 plots the probability of having a
second child (conditional on having a first birth) from 1975 through 1981 for ten
age groups (20-29). Similarly, Figure 2.9 shows the probability from 1975 through
1989 using the 1990 sample. All the table and figures present the results for Han
and minority women separately.

The main analysis has used an identification strategy based on a policy feature
that the one-child quota only applies to the Han Chinese but. not minorities. If this
is the only thing that has caused different fertility behavior between them, we
should expect to observe a similar trend in second-birth giving for Han and
minority women before 1979, and then a relatively larger decline among Han
women around 1979. However, at least for the 20—24 groups, this is not the case
shown in Figures 2.8 and 2.9. The graphs clearly indicate that the pre—1979 trends
in fertility were already much different between the two ethnic groups. For most
age groups of Han women, their fertility kept falling between 1975 and 1979, while
this pattern was not seen for minorities. Moreover, it seems that the 1979 policy
has had little effect on deterring the second birth of Han women. The fertility of
Han women continued to decline a few years after 1979 but remained more or less
at the same level since the early 19805. Given the sharp drop in fertility starting
prior to 1979, the figure would suggest that the policy has eased (or even reversed)

rather than hastened the declining trend.

85

The graphical analysis here provides some evidence invalidating our identifying
assumption that the Han Chinese and minorities should have similar changes in
fertility with the absence of the affirmative birth control policy. Therefore,
attributing all of the [Ian-minority gap in fertility found in the paper to the one-
child policy cannot. be justified. There have to be some other socio-economic
factors or policy changes that have caused the Han-minority difference in fertility

behavior.

86

.15

3*
.
. .
i t
:0
.

u:
o.

.15

Figure 2.8: Probability of Having a Second Child by Year (1982 Census)

A: Han 20-24

on

 

    

 

I I I I
1975 1976 1977 1978

I

1979

 

_..—
._——..____

 

20
22
24

—6—- 21
,__..4'..._ _ 23

 

 

C: Han 25-29

.1

 

IN/

1-46“" ' I

_. - ”~41- " "

A.
‘.
T__+-_—+__X——T __ _.__._.___.__..___

/

I

/

1| 1"

J

I f
1980 1981

 

I I I I I I I
1975 1976 1977 1978 1979 1980 1981

 

_._

-+ --

 

-———~w—“

25
27
29

+26
~28

 

 

87

 

B: Minority 20-24

     

 

 

 

 

 

 

 

 

N- l
' I
1
I
4'
/ "|\.-
l
1
mod I
I
l
I
I
l
I
I
l
'd l
I
I
I
I
l
I
I
l
34 l
I I ‘I I l I I
1975 1976 1977 1978 1979 1980 1981
—o—- 20 —e— 21
——4I—-— 22 Wren—— 23
. _,1-,_.,.. 24
D: Minority 25-29
01—1 1
' I
l
I
I
I
I
l
I
a. l
' 1
M
m
I
I
‘7‘ l
I
I
I
_ ..~—,.'o."' \ '
.. --~+——~ .. ~
c>_- 1
)4... W‘ $4 |
I I I 1 IL I I
1975 1976 1977 1978 1979 1980 1981
+ 25 —0— 26
-—*—- 27 ----:~--- 28
._..,¢'.._._ 29

 

 

 

 

0‘

Figure 2.9: Probability of Having a Second Child (1990 Census)

A: Han 20-24

 

ll)

 

O

B: Minority 20-24

 

 

 

    
     

3-

 

C: Han 25-29

 

 

In

 

D

   

4. x

I
,4 av

 

 

 

88

‘-1 r I r F f *F
1975 1977 1979 1981 1983 1985 1987 1989

 

Table 2.7: Descriptive Statistics: 1982 and 1990 Censuses

 

Mean and (standard deviation)

 

 

 

 

 

 

1982 Census 1990 Census
All Han Minority All Han Minorit
women Women y
Variable (l) (2) (3) (4) (5) (6)
Number of 2.15 2.14 2.47 1.89 1.87 2.20
children (1.06) (1.04) (1.28) (0.93) (0.91) (1.11)
Having 2 or more 0.685 0.682 0.743 0.599 0.591 0.709
children (0.465) (0.466) (0.43 7) (0.490) (0.492) (0.454)
H 11 0.950 _ 0.936 _
a (0.218) ' (0.245)
A c 29.0 29.1 28.6 31.3 31.3 30.6
g (3.6) (3.5) (3.8) (5.3) (5.2) (5.3)
. 22.8 22.9 22.4 23.2 23.2 22.8
Age at fir“ hm" (2.7) (27) (2.9) (2.7) (2.7) (2.9)
aftiitigecond 24.6 24.6 24.4 25.6 25.6 25.2
applicable) (2.7) (2.7) (2.8) (3.2) (3.2) (3.3)
Sample size 604,242 573,937 30,305 1,158,872 1,084,384 74,488

 

Notes: The samples include women aged 20-35 (20-40 for 1990) who were household head or
spouse of the head, had been married by the time of the census, and had at least one child.

89

 

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93

 

Chapter 3

Child Care Subsidies and Employment of Single Mothers

94

1 Introduction

The US. welfare system changed dramatically during the 19908, beginning with various
state-implemented experimental programs and culminating in the passage of the Personal
Responsibility and Work Opportunity Reconciliation Act (PRWORA) in 1996. In order to
reduce dependence of needy parents upon welfare and promote their work participation,
perhaps one of the biggest shifts in welfare reform is the emphasis on providing work incen-
tives to low-income families with children (many of which are headed by single mothers).
Part of these efforts were substantial changes in the child care assistance programs that
subsidize child care costs of low-income parents while they participate in work or training.1
The PRVVORA consolidated four earlier different child care subsidy programs into a single
block grant called the Child Care and Development Fund (CCDF). States were also allowed
to transfer up to 30 percent of their cash assistance block grants (Temporary Assistance for
Needy Families (TAN F )) into CCDF or spend TANF directly on child care. In addition,
the CCDF gave states a great deal of flexibility in setting subsidy program rules, such as
income eligibility ceilings, family copayment levels, and reimbursement rates to providers.

The restructuring of the subsidy programs has led to a significant increase in federal
and state funding for child care. In fiscal year 2005, $4.8 billion in CCDF was available
through block grant funding, more than double the $2.2 billion available in 1996. Combined
with state matching, TANF dollars transferred to CCDF or spent directly by states, and

other funding sources, a total of $11.4 billion was available for child care in 2005, more

 

1The programs discussed here provide subsidies for work—related child care expenses of chil-
dren in low-income families. Other federal and state programs, such as Head Start and state
prekindergarten programs, also assist low-income parents in caring for and educating their chil-
dren. Generally these programs have no employment requirements and have different goals than
child care subsidies. Although they in effect provide subsidized high-quality child care to many
low-income children, they do not fall within the conventional definition of “child care subsidy” in
the literature.

than triple the $3.6 billion in 1996. In an average month in 2005, 1.75 million children
(1 million families) received child care services through these funds (Child Care Bureau
(CCB), 2006a). \Nith the expansion of financial assistance for child care, policymakers
and researchers have been eager to understand the relationship between the use of child
care subsidies and parents’ (especially mothers’) employment outcomes, sparking a growing
body of research on this issue.

Some of the first literature related to child care subsidies examines the effect of the
price of child care on mothers’ employment and child care selection, and then uses the
estimated responses of labor supply with respect to child costs to infer the impact of
child care subsidies. Anderson and Levine (2000), Blau (2003), and Blau and Currie
(2006) summarize these studies and conclude that differences in econometric specification
and estimation play an important role in producing the wide variation in the estimates.
Moreover, this literature may suffer from an important identification difficulty: factors
affecting child costs (such as number of children or local wages) may covary with unobserved
determinants of labor supply.

Several recent studies have tried to isolate exogenous variation in child costs to identify
employment responses. Gelbach (2002), Chiang (2008), Fitzpatrick (2008), and Cascio
(2009) all focus on the implicit subsidy provided by early education programs. With
different identification strategies, they estimate the effects of young children’s enrollment
in public school on maternal labor supply and generate mixed findings for different groups.
Baker et al. (2008) and Lefebvre and Merrigan (2008) both analyze the policy effects of
a universal subsidized child care program introduced in Quebec in 1997, and find that the
program significantly increased mothers’ labor supply. But as these results are based on
either implicit subsidies or universal child care, they are not necessarily a good guide to

96

the effects of explicit child care subsidies or subsidies that are only available to certain
population (such as low-income people).

Another strand of literature has directly examined labor supply responses to actual
child care subsidies and largely found positive subsidy effects (Berger and Black, 1992;
lV‘Ieyers et al., 2002; Tekin, 2005; Blau and Tekin, 2007; Tekin, 2007)? The former two
studies use data prior to welfare reform from child care subsidy programs in Kentucky
and California respectively, while the latter three all draw on a sample of single mothers
using postreform survey data from the National Survey of America’s Families (N SAF). A
typical specification in this literature is to estimate the effect of the actual subsidy receipt
on the employment outcomes of mothers. and some try to account for the endogeneity of
subsidy receipt using instrun’ients such as mothers’ knowledge of program rules (Meyers
et al., 2002), state CCDF spending (Tekin, 2005). or county dummies (Blau and Tekin,
2007)

Given that states have substantial flexibility in designing their CCDF programs, surpris-
ingly few studies have explored the variation in child care subsidies along this dimension——
whether and to what extent the generosity of state child care programs affect the labor
supply and subsidy receipt of low-income parents. To this end, this paper attempts to fill
in the gap by examining the impact. of child care subsides on outcomes of single mothers
in a postreform period. Such exercise can provide direct answers to policymakers’ interest.
in whether these child care programs have achieved the goal of supporting the employment.

of low-income parents.

 

2Besides, Robins (2007) reviews a number of experimental welfare reform programs between
1989 and 2002 that include child care subsides along with other employment-related benefits and
services. Although these programs are found to have significantly increased employment, it is
hard to disentangle the treatment effects of child care subsidies from the overall program effects.

97

The paper makes use of policy data on family copayments and provider reimbursement
rates from 2001 through 2007 to construct the implied child care subsidy offered by each
state to parents of a preschool age child. The subsidy information is then linked to a sample
of single mothers of young children from the Current Population Survey (CPS) to estimate
the subsidy effects on mothers’ subsidy receipt and employment. The results suggest that
higher subsidies have a weak effect on promoting the use of subsidies or encouraging work
participation among single mothers, although subsidies appear to have a small effect on
increasing full-time employment.

The remainder of the paper is organized as follows. Section 2 provides background of
child care assistance (CCDF) programs. Section 3 describes the data. Section 4 presents
the economic framework and the estimation results. Section 5 discusses the results and

concludes.

2 Child Care Assistance Programs

Child care subsidies help low-income families pay for the care and education of their chil-
dren while parents work and/or participate in education and training. The rationale for
government-subsidized child care is based on three arguments: to attain economic self-
suffieiency, to improve equity, and to correct child care market imperfections (Blau, 2003).
Encouraging low-income parents to work can help them become economically self-sufficient
(i.e., employed and unattached to welfare). If current self-sufficiency can increase future
self-sufficiency by fostering work ethic and accumulating human capital, it may save the
government spending on welfare assistance in the future (Robins, 1991).

The 1996 passage of the PRWORA restructured the child care assistance programs by

repealing three Title IV—A programs and the Child Care and Development Block Grant,

98

 

whose funding streams were then consolidated into the single CCDF. There are three pri-
mary elements to CCDF funding (CCB, 2006a). First, each state receives a pre—determined
share of federal mandatory funds, which remains constant over time. Second, states can
qualify for matching grants if they meet certain Maintenance of Effort requirements (i.e.,
keep or exceed pre-CCDF spending levels). Finally, the legislation distributes discretionary
funds that do not need a state match.

By statute, the eligibility for CCDF subsidies is determined along three dimensions: the
age of the child, parental employment status, and family income (CCB, 2006a). Generally
speaking, CCDF services are provided up to age 13, or age 19 for children who are under
court supervision or are mentally or physically incapable of self-care. States may serve
families when parents are working (including both formal employment and job search
activities), in education or training, or when children are receiving protective services.
The income level of such families may not exceed the eligibility levels set by the state
and the federal maximum of 85 percent of the State Median Income for a family of the
same size. States may also define and give priority to children with “special needs” and to
children from “very low-income” families.

The subsidy benefits are largely regulated by copayinent and reimbursement policies.
Families receiving a CCDF subsidy are allowed to choose any legally operating child care
provider who has a grant or contract to provide services or to receive a child care certificate
(voucher).3 Parents are required to contribute to the cost of care on a sliding-fee basis,

which is typically based on family size and income. The fees are set to rise with income

 

3The regulations define child care provider as one who provides child care in a center, a group
home. a family home, or in the child’s own home. A certificate or voucher is defined as a check
or other disbursement that is issued by a state or local government directly to a parent who may
use the certificate only as payment. for child care services. Certificates must be flexible enough to
allow funds to follow the child to any participating child care provider the parent selects.

99

to phase out subsidies, and some states allow copayments to be waived for families below
or at the federal poverty level. Reimbursement rates, the maximum amount states will
pay a given child care provider, represent the maximum amount of the subsidy exclusive
of the family copayment. The rates may vary depending on child age and the type of care.
States conduct market rate surveys periodically to ensure that subsidized families have
“equal access” to high—quality providers, which are defined as reimbursement levels that
cover 75% of the local child care price distribution and copayments that do not exceed 10%
of family income (CCB, 2006a).

Unlike its predecessor programs, the CCDF does not administer benefits as an entitle-
ment. One important feature of the CCDF is that. states are allowed substantial freedom
to determine rules governing eligibility and benefits. As a result, many states use eligibility
rules and other administrative functions to change the availability of subsidies, especially
when they cannot meet. the demand for subsidies due to fiscal constraints. Some may
choose not to provide child care assistance to all eligible families who apply by placing
them on waiting lists or freezing intake. Some may continue to serve all eligible applicants

but also raise their copayments or lower the reimbursement rates at the same time.

3 Data
3.1 Child Care Subsidies

The value of the child care subsidy to the family depends on the family copayment and the
rate of provider reiml:)ursement. The data on these policies are provided by two sources.
The information on parent copayment levels is taken from annual policy surveys conducted
since 2001 by the Children’s Defense Fund (Children’s Defense Fund, 2004) and the Na-

tional Women’s Law Center (Schulman and Blank. 2004-2007). The data. on reimbursement

100

 

rates are contained in the CCDF plans submitted by states to the federal government bi-
ennially (CCB 2001, 2002, 2004, 20061)). It is worth mentioning that the rates reported
in the state plans were not updated annually because the adjustment was usually based
on the market rate surveys conducted every two years.4 This means that in years (2003,
2005, and 2007) when reimbursement rates were not updated, the variation in child care
subsidies entirely came from the changes in copayments.

The measure of the. child care subsidy is constructed as the difference between the reim-
bursement. rate (the maximum provider payment) and the family copayment, which implies
the net value of the maximum subsidy. As copayments can vary by family income and re-
imbursement rates can vary by child age and the type of care, given the data available,5
the child care subsidy here represents the maximum subsidy for a preschool age child who
is in full-time care at a center-based facility and from a family with income at the federal
poverty level.

To have some sense of how the poverty line can describe low-income families, Table 3.6
in the Appendix compares the poverty guideline for a single—parent family (one parent and
one child) with the hypothetical earnings of the parent assuming that he or she works 40
hours per week at the state minimum wage rate- The poverty line falls into the range of
the minimum-wage earnings and is higher by roughly 10% than the income that can be
earned at the average minimum wage across all states. Considering that copayments are

usually set to rise with income and do not exceed 10% of the income, this suggests that on

 

4It is likely that some states modified the rates within the two-year period before the next plan
was submitted, but complete data on annual reimbursement rates are not available.

5The copayment data do not provide the complete sliding-fee schedule but only the fees for
families at 100% and 150% of the federal poverty level. Because families at 150% of poverty are
not always eligible for subsidies in all states, the fee for families at 100% of poverty is used here.
Reimbursement rates can also vary by region within a state. In that case, the state plans reported
the rate in the largest urban area.

101

average the child care subsidy for a family at the poverty line is slightly lower than that
for a family headed by a full-time minimum-wage earner.

The variable measuring the child care subsidy (in 2007 dollars) is summarized in Table
3.1 and its distribution (in both level and change) is plotted in Figure 3.1 in the Appendix.
They both show a fairly large amount of variation across states, suggesting that states have
substantial flexibility in designing their policies. The child care subsidy ranges between
$172 (Louisiana) and $1,251 (Minnesota), with an average of $489 (ad. = $205). On the
other hand, the variation over time appears relatively small. Although each year roughly
between one-half and three-quarter .- of the states adjusted their policies, the amount of
changes was not very large, as suggested by the spikes of changes close to zero in Figure
3.1.

To check whether the measure of the child care subsidy can indeed capture the gen-
erosity of the CCDF programs, it may be useful to examine the correlation between the
subsidy and other measures of generosity in the state. Column 1 in Table 3.2 estimates the
relationship between the average CCDF expenditure on a child receiving the service and
the child care subsidy.6 The regression shows that. child care subsidy is positively correlated
with the average CCDF expenditure. The point estimate suggests that a $1 increase in
the subsidy would turn into a $0.17 increase in the state’s expenditure on an average child.
Column 2 regresses the total CCDF expenditure on the number of children served by the
system, and the point estimate suggests that on average, serving one additional child would
increase the C CDF expenditure by $125 per month. This figure is smaller than the average

child care subsidy summarized above. But. note that the subsidy measure is based on the

 

6The data on CCDF expenditures and the number of children in services, which are available
on-line at http://www.acf.hhs.gov/programs/ccb/data/index.htm., are provided by the Child
Care Bureau.

102

 

maximum provider payment and in practice states may pay providers by the amount less
than the ceiling. Furthermore, the child care subsidy for a preschool child in a family with
income at the poverty level may more closely measure the subsidy for families at the higher
end of the subsidy range. This is plausible because the income at the poverty line tends
to be at the lower end of the income range and so does the family copayment, given that
the average income eligibility level (about $29,100) is well above the poverty line and that

some states also waive copayment. fees for families below or at the poverty level.

3.2 Other Data

Because it is plausible that states are coordinating their various policies to encourage
employment of low-income people, it is necessary to control for other factors that could
potentially confound the estimated effects of child care subsidies. Therefore, some other
measures of welfare policies, which are taken from the Urban Institute’s Welfare Rules
Database.7 are also included in the analysis. Basically these policies are intended to capture
the work-related requirements and the generosity of the welfare environment in a state.
Specifically, the variables include the maximum cash benefit, the minimum number of
hours required for a single parent on welfare (classified as no requirements, moderate
requirements for 18—30 hours per week, and high requirements for 32 or more hours per
week), whether a full-family sanction was imposed for violation of work requirements, and
whether a lifetime termination time limit was in effect. The state unemployment rate is
also included to control for local labor-market opportunities.

The policy data are linked to a sample of single women from the CPS data who are not in

school and have at least one child younger than 13.8 The main variables of interest are use

 

7Available on-line at http://anfdata.urban.org/wrd/wrdwelcome.cfm.
8Married women are not studied here because single-parent families are the most commonly

103

 

of child care subsidy and employment status. The subsidy receipt is analyzed to detect the
mechanical effects of child care subsidies, i.e., whether higher subsidies would attract more.
women to participate in the programs. The employment outcomes are used to estimate
the behavioral effects on work participation in response to the work incentives provided by
child care subsidies. Since 2001 the survey began to ask whether the respondent received
any child care assistance from a state or county welfare agency so that the respondent could
go to work, school, or training. This helps identify the subsidy receipt. For employment,
the analysis examines any type of work (positive work hours) and full-time work (35 hours
or more per week) respectively.

The sample contains 30,300 women and Table 3.3 provides the descriptive statistics for
the full sample and two subsamples by whether the mother received child care assistance.
Among all mothers, 67 percent were employed and 51 percent were full-time workers.
Approximately 10 percent. of them received child care assistance. This rate is between
the one (8%) reported by Tekin (2007) and the one (12%) reported by Blau and Tekin
(2007), both of whom use a sample of single mothers from the NSAF data but of different
sampling years. To see whether the measure well identifies parents who received child care
assistance, column 3 in Table 2 reruns the regression as in column 2, but with the number
of receipts estimated based on the CPS data as the dependent variable. The coefficient
is close to that in column 2, suggesting that the variable in CPS is a fairly good measure
of who were receiving child care subsidies. The statistics on other characteristics of the
women are very close to those reported in other studies that are also based on samples of

single mothers with young children (see. e.g., Meyer and Rosenbaum, 2001; Tekin, 2007).

 

seen families using subsidies. According to the CCDF administrative data, more than 85% of
families receiving subsidies were headed by single parents (CCB, 2006a).

104

 

Comparison of the two subsamples first shows that the subsidy recipients were more
likely to be employed (by 9 percentage points) and be full-time employed (by 3 percentage
points) than nonrecipients. This is not. surprising given the requirements of work-related
(including job-seeking) activities imposed on subsidy receipt by welfare agencies. In ad-
dition, compared to nonrecipients, subsidy recipients were more likely to have younger
children below 6 years old (by 24 percentage points) and an average recipient also had a
larger number of younger children. This presumably reflects a greater need for non-parental
child care among these children.

Turning to educational attainment, it seems surprising that subsidy recipients were
less likely to be high school dropouts or graduates and more likely to have some college
education (but not a bachelor degree), as the CCDF programs are expected to be targeted
at low-income women who tend to be less educated. However, this observation echoes the
finding in the literature that the likelihood of receiving a subsidy is greater among those
with relatively high levels of education. For example, Blau and Tekin (2007) find that.
mothers who have completed high school or had attended some college are more likely
to receive a subsidy (by 3 percentage points) than high school dropouts. Herbst (2008)
reaches the same conclusion that the subsidy receipt among single mothers is positively
associated with high school graduates or some college education. One interpretation is that
women already at work (but not earnng too high to become ineligible for the subsidy) may
have better knowledge of the subsidy and seek for it more actively. Another explanation
is that conditional on being eligible, states may favor individuals with better skills over
those with potential barriers to employment in order to facilitate the improvement of work
participation rates. In other words, states’ targeting practices are meant to “cream” the
eligible population for high-skilled workers (Herbst, 2008).

105

Fm.

‘4

 

'1.

4 Estimation

4.1 Work Incentives in Child Care Subsidies

Child care subsidies generally increase a parent’s incentives to be employed. This can be
shown using a simple static one-person labor supply model augmented with assumptions
about child care (Blau, 2003). For simplicity, the model assumes that there is only one
child who needs care, and child care is homogeneous in quality and commands a market
price of p dollars per hour of care. There is no informal unpaid care available and the
mother cannot care for the child while she works. so paid care is required for every hour
the mother works. Similarly, by assumption the mother cares for her children during all
hours in which she is not working.

The mother maximizes her utility U (C , L) subject to the budget constraint C = Y +
(w — p)H and the time constraint H + L = 1, where C is the consumption of market
goods, L is hours of leisure, H is hours of work, Y is nonwage income, and w is the
wage rate. An increase in the price of child care will reduce the likelihood of employment.
because it increases the likelihood that the net wage rate (in — p) is below the mother’s
reservation wage. Likewise, a child care subsidy of 3 dollars per hour would raise the net
wage (w — p + 3), make the slope of the budget line in consumption-leisure space steeper,
and hence increase the likelihood of work. However, the effect of such a subsidy on hours
of work conditional on being employed is indeterminate because the subsidy has a positive
substitution effect and a negative income effect on hours simultaneously.

This simple model can be extended to incorporate more complicated issues such as
nonlinear subsides and the use of unpaid care. As most states structure their sliding-fee

scale to have increasing copayments as family incomes rise and impose a maximum income

106

 

 

level of eligibility, this suggests a subsidy rate declining with income and thereby a nonlinear
budget constraint. Compared to the linear subsidy above, a nonlinear structure does not
change the qualitative result that a subsidy would encourage more employment, though it
could affect the incentive to locate at any particular positive level of hours worked (Blau,
2003)

Blau (2003) also considers another case that the mother can use some unpaid care, which
is typically provided by other family members. But such care usually has an opportunity
cost (the leisure or earnings given up by the provider) and the mother needs to balance
between paid and unpaid care. A child care subsidy reduces the effective price of market
care but does not affect the price of unpaid care. In this case, Blau shows that in addition
to providing a work incentive, a subsidy also makes the mother more likely to use paid
care conditional on she is working. Therefore a subsidy to market care can “crowd out”
private care.

In any case, the model predicts that the introduction of a child care subsidy would
increase the incentive to be employed. The intuition is that a subsidy reduces the cost
of child care when the mother is employed, but has no impact on utility when she is not
employed. The conclusion also holds when the model is further extended to allow for
variable quality in child care, and it can be shown that a subsidy that is independent of
quality will have a bigger positive effect on employment than a subsidy that is quality-

specific (Blau, 2003).

107

.17

 

4.2 Effects of Child Care: Subsidies

This subsection empirically tests how the generosity of state CC DF subsidies affects women’s

subsidy receipt and employment status. The regression model is specified as:
Yst = (l + JiSltbSt + fléxst + 7’5 + At + Est, (1)

where Yst is one of the outcomes of interest, and Subst is the measure of state child care
subsidy. The model controls for individual characteristics and other state welfare policies
(both included in X31) described in the data section, as well as year (A1) and state (75)
fixed effects. The year indicators are intended to pick up changes in outcomes that are
constant across states but vary over time. The state effects attempt to capture unobserved
heterogeneity that are assumed to be common within a state over time. A linear probability
model is estimated, with the standard errors corrected to allow for an arbitrary correlation
within states.

The main estimation results are presented in Table 3.4.9 The estimates first indicate
that the child care subsidy has weak effects on both subsidy receipt. and overall employ-
ment, as the coefficients (columns 1. and 2) are small in Iriagnitude and not statistically
different from zero as well. The point estimates suggest that a $100 increase in the subsidy
would increase the receipt by 0.3 percentage point and increase en‘iployment by 0.3 per-
centage point. Given that 10% of these women received subsidies and 67% were working,
the induced increases are quite small. The estimate for full-time employment in column 3
suggests a significant effect of the subsidy. A 8100 increase in the subsidy would increase

full-time work by 1.2 percentage points, which imply a percentage change of 2.4% (1.2/ 51).

 

9To see whether the estimates of the child care subsidy are seriously confounded by other state
work-related policies, Table 3.7 in the Appendix runs the regressions without controlling for other
policy variables. The results are very similar.

108

 

These findings suggest some employment responses at the intensive margin but little re-
sponses at the extensive margin. However, since child care subsidies are mainly picking up
the incentives that. are expected to affect participation decisions (the extensive margin),
the significant effect on full-time employment implies that the subsidy may also capture
some other incentives that could influence labor supply (the intensive margin). This im-
plication is interesting and deserves further study that includes both work incentives for
the extensive and intensive margins.

The estimates of other welfare policy variables are also reported in Table 3.4.10 Both
state unemployment rate and maximum cash benefits are positively associated with subsidy
receipt and negatively associated with employment, but none of the coefficients on these
two variables are precisely estimated. Work hour requirements appear to have strong
effects on receiving subsidy and work participation. The coefficients suggest that, relative
to the reference category of no hour requirements, moderate requirement (18-30 hours)
would increase the subsidy receipt by 2.5 percentage points and overall employment by 3.2
percentage points, and high requirements (32-40 hours) would increase overall employment
by 6.8 percentage points and full-time employment by 9.9 percentage points. The large
effects of high requirements represent increases of approximately 10% and 20% in overall
and full-time employment. Finally, the effects of sanction policy and termination time
limit are small and statistically insignificant through all regressions.

The above analysis has compared the changes in mothers’ outcomes in states that

adopted various child care policies. Given that states may choose to target families who

 

10The mother covariates, though not reported, exhibit the similar patterns as shown in Table 3.3.
Consistent with previous literature on determinants of child care subsidy receipt, the likelihood
of receiving a subsidy is greater among women with a larger number of young children as well as
those with relatively high levels of education. On the other hand, the work participation increases
with educational attainment and decreases with the number of young children.

109

 

'1

 

are in greater need of child care to support parents’ work, it is possible that some mothers
are more likely to be affected by the subsidies while some others respond little to the
program change. In this case, the policy effect. can be better measured by comparing the
affected individuals to a set. of unaffected individuals in the same states and then comparing
the changes in such relative outcomes across states that experienced various policy changes.
This approach can control for some unobserved state-specific shocks varying over time that
may be correlated with child care subsidies and thereby bias the estimates.

To test this possibility, Table 3.5 reports the estimates from a model that assumes
mothers with children younger than 6 years old to be the affected group. In general
these women should be in greater need of subsidized care and the previous results have
shown a positive correlation between the subsidy receipt and the presence of a younger
child. Nonetheless, the coefficients do not suggest a much different story from that of the
baseline model. The primary effects of the child care. subsidy (the first row) are very similar
to those estimated in Table 3.4. Meanwhile, the subsidy does not appear to have significant
effects on increasing subsidy receipt or employment for those women with younger children,
as suggested by the coefficients on the interaction between the subsidy and the child age
indicator. The findings imply little difference in how mothers of younger children were

affected by the child care subsidy.

5 Conclusions

As an important part of welfare reform, child care subsidy programs and funding for such
subsidies have grown rapidly in the past. decade. Yet, there is little information about
whether child care subsidies have in fact contributed to the goal of the programs, i.e., to

support the employment of low-income parents.

110

 

lifi'n‘

Relying on the fact that the CCDF gives states great flexibility in designing and ad—
ministering their child care programs, this paper uses data from 2001 through 2007 to
test whether the state—set subsidies have affected the receipt of subsidies and employment
outcomes of single mothers. This is one of the first studies that make use of the variation
in the state CCDF programs to examine the subsidy effects on employment. The results
suggest little effect of child care subsidies on the likelihood of receiving subsidies or being
employed, though higher subsidies are found to slightly increase full-time work.

To relate these findings to previous research, first the more common but less direct evi-
dence comes from the studies of the effects of the price of child care on employment. While
it remains debatable whether the price effects may be a reliable guide to subsidy effects
(Blau and Tekin, 2007), most studies find that a higher price reduces employment but the
elasticity estimates vary substantially (from 0 to ~1.26, with some clustering between —0.3
and -0.4). After a detailed examination of specification and estimation differences across
these studies, Blau and Currie (2006) find that the estimates from those using arguably
more exogenous variation in child care costs tend toward the lower end of the range, and
hence conclude that “... the best available estimates suggest that the effects of the price
of paid child care on labor force participation... are small.”

A smaller body of literature has linked the actual receipt of child care subsidies to
employment outcomes. Both drawing on a cross-sectional sample of single mothers in
the postreform era, Blau and Tekin (2007) and Tekin (2007) provide the most relevant
evidence. The former study finds that state policies (including the CCDF policies) have
no significant effects on the subsidy receipt, and that receiving subsides is associated with
higher employment. However, the subsidy effect on employment is likely to be biased
given their difficulty in finding convincing instruments to identify the subsidy receipt.

111

Tekin (2007) examines the effect of child care costs on employment after incorporating the
subsidy receipt into the mother’s choice set and adjusting the price of child care by the
subsidy. His results suggest a small elasticity (—0.12) of overall employment with respect
to the the price of child care, and that the elasticity for full—time employment is larger
than that for part—time employment. On the whole, the finding of this study that child
care subsides have little effect on subsidy receipt or overall employment is in line with the
existing evidence suggesting small effects of child care costs on work participation, but
the estimated response of full-time employn'ient seems to be smaller than what Tekin and
others find.

Further, as child care subsidy programs are part of the welfare system that. has been re-
formed to create various work incentives to promote work participation among low-income
individuals, it is also important to compare this study to other research on government pro-
grams that offer similar wage—supplement benefits to low-income families. Few studies have
provided directly comparable evidence regarding federal or state child care programs. The
only exception is Meyer and Rosenbaum (2001), who evaluate the impact of pre-PRVV ORA
child care programs (among other policies) on the employment of single mothers between
1984 and 1996. Their results indicate that. a monthly $100 increase in federal and state
child care expenditures per mother is associated with about a 2.1 percentage point increase
in employment. This is close to the size of the effect (though not statistically significant)
estimated in this paper, as calculation using coefficients from column 1 in Table 3.2 and
column 2 in Table 3.4 suggests that an increase in the CCDF expenditures of the same
amount is associated with an increase in employment by approximately 1.8 percentage
points (0.3/0.166).

However, other types of wage-supplement benefits, such as welfare payments to working

112

recipients and the Earned Income Tax Credit (EITC), appear to have larger effects than
child care subsidies. For example, h‘leyer and Rosenbaum (2001) find that a $100 reduction
in income taxes if a women works would increase employment by 2.5 percentage points,
and that a $100 increase in benefits when she works would increase employment by 7
percentage points. Similarly, Grogger (2003) finds that a $100 increase in the maximum
EITC credit results in a 3.4 percentage point increase in the employment of single women.
All the estimates are considerably larger than the child care subsidy effect (0.3) found in
this study.

One potential reason for the weak responses to child care subsidies could be the low
rates of participation in child care programs among eligible parents. Even with the signif-
icant expansion of financial assistance for child care, the national estimates suggest that
only 12% to 15% of eligible children received assistance (CCB, 1999; General Accounting
Office, 1999). The most common barriers to receiving subsidies are lack of awareness and
difficulties navigating the system (Schlay et al. 2004). Many eligible nonrecipients are
unaware of their eligibility, and some others do not apply for subsidies because of the mis-
perceived hassles to obtain and retain subsidies. Sometimes certain prospective applicants
may be reluctant to apply for subsidies after they become aware of the states’ targeting
policies and believe that. they would not receive priority. If only a small proportion of
eligible mothers (the proportion should be lower among all single mothers because some
women are ineligible due to income or other reasons) take into account of receiving child
care subsidies when making employment decisions, this could lead to a small overall subsidy

effect.

113

Table 3.1: Summary Statistics on Child Care Subsidies by Year

 

Maximum monthly child care subsidy for a preschool age child at a center-
based facility and from a family with income at federal poverty level

 

 

# of

States Mean (SD) Min Max
2001 48 480.5 (192.9) 240.9 1,109
2002 46 524.6 (207.6) 256.4 1,215
2003 46 507.7 (204.8) 196.9 1,162
2004 50 493.8 : (212.0) 177.5 1,251
2005 50 478.5 (210.2) 171.7 1,208
2006 50 481.4 (208.7) 196.9 1,178
2007 50 460.9 (201.3) 176.5 1,144
All 340 489.0 (204.6) 171.7 1,251

 

Notes: The amount of subsidy is in 2007 dollars. Subsidies are calculated based on the family copayments
and reimbursement rate set by states. In case the reimbursement rate varies by region within the state, the

rate in the largest urban area in the state was reported. Source: Child Care Bureau (2001, 2002, 2004,
2006b), Children’s Defense Fund (2004), and Schulman and Blank (2004-2007).

114

 

Table 3.2: Child Care Subsidy and CCDF Expenditure

Dependent variable in OLS regression

 

 

CCDF expenditure per Total CCDF expenditure
child served
(1) (2) (3)

Child care subsidy 30106965,; - -
Number of children served by - 124.9*** -
CCDF (24.3)
Number of parents receiving - 94_0***
services based on CPS data (31.5)
Year FE Yes Yes Yes
State FE Yes Yes Yes
R-squared 0.59 0.97 0.97
Sample size ,. 340 340 340

 

 

 

Notes: *, **, and *** represent significance levels of 10, 5, and 1 percent. Standard errors clustered by state
are shown in parentheses. The variables are described in Table 1.

115

 

Table 3.3: Descriptive Statistics on Single Mothers with Children under 13

All

Received child care

No child care

 

Variable (1 ) assistance assistance
(2) (3)
Child care subsidy 477.6 ( 194.5) 479.8 (198.8) 477.4 (194.0)
Employed 0.666 (0.472) 0.747 (0.435) 0.657 (0.475)
Full time employed 0.507 (0.500) 0.531 (0.499) 0.504 (0.500)
Unemployed 0.084 (0.277) 0.096 (0.294) 0.083 (0.275)
Nonwage income 3,991 (7,165) 4,055 (6,523) 3,984 (7,234)
Age 32.7 (8.1) 29.8 (6.7) 33.0 (8.1)
At least one child under 6 0.521 (0.500) 0.744 (0.437) 0.496 (0.500)
# of children under 6 0.68 (0.76) 1.02 (0.79) 0.64 (0.75)
# ofchildren aged 6-12 0.95 (0.84) 0.88 (0.89) 0.96 (0.83)
Black 0.269 (0.443) 0.297 (0.457) 0.266 (0.442)
Hispanic 0.185 (0.388) 0.128 (0.334) 0.192 (0.394)

High school dropout
High school

Some college
Bachelor

Number of observations

0.213 (0.410)
0.392 (0.488)
0.318 (0.466)
0.077 (0.267)

30,300

0.168 (0.374)
0.388 (0.487)
0.392 (0.488)
0.052 (0.222)

3,067

0.218 (0.413)
0.392 (0.488)
0.310 (0.463)
0.080 (0.271)

27,233

 

Notes: Standard deviations are shown in parentheses. Data are from CPS March Supplement 2001-2007.

116

Table 3.4: OLS Estimates of the Effects of Child Care Subsidy and Other Policies

 

Dependent variable

 

Received child care

 

assistance Employed Full-time employed
(1) (2) (3)
. . . 0.003 0.003 0012*"
Child care subsndy (in 100) (0.003) (0.003) (0.005)
0.002 -0.007 -0.003
Unemployment rate (0. 006) (0' 006) (0. 006)
Maximum benefits (in 100) (33%?) (.8883) (.8883)
Moderate hour requirement 0025*" 0.032" 0.017
(18-30) (0.008) (0.013) (0.016)
High hour requirement 0.018 0068*" 0099*“
(32-40) (0.01 1) (0.018) (0.021)

. . -0.005 0.003 0.002
Full-family sanction (0‘0”) (0.010) (0.016)
Time limit 0.004 -0.029 -0.009

(0.015) (0.026) (0.019)
R-squared 0.06 0. 17 0.16

 

Notes: *, **, and *** represent significance levels of 10, 5, and 1 percent. Standard errors clustered by
state are shown in parentheses. All regressions control for mother’s characteristics as listed in Table 3, and
both year and state fixed effects. N = 30,300.

117

 

Table 3.5: OLS Estimates of the Effects of Child Care Subsidy by Child Age

 

Dependent variable

 

Received child care

 

assistance Employed F ull-time employed
(1) (2) (3)
. ‘ . . 0.002 0.003 0.01 1”
Child care subSIdy (in 100) (0.002) (0.006) (0004)
Unemployment rate 0.001 -0.005 -0.003
(0.005) (0.011) (0.011)

. . -0.001 0.0005 -0.005
Max1mum benefits (in 100) (0.006) (0.014) (0.014)
Moderate hour requirement 0040*" 0.031" 0.028
(18-30) (0.008) (0.012) (0.022)

High hour requirement 0037*" 0064*" 0100*"

(32-40) (0.010) (0.014) (0.027)
Full-family sanction 0'006 '0'012 00%
(0.015) (0.020) (0.016)
Time limit -0.005 0.020 0.052“
(0.014) (0.021) (0.021)

. . . 0.002 -0.005 0.005

*
Child care subsrdy child<6 (0.004) (0.007) (0.009)
. 0.001 -0.005 -0.001
*
Unemployment rate child<6 (0.006) (0.013) (0.013)
. . 0.004 -0.008 0.003
*
Maxrmum benefits child<6 (0.009) (0.018) (0.022)
Moderate hour requirement * -0.030*** -0.003 -0.026
child<6 (0.010) (0.019) (0.023)
High hour requirement * -0.033* -0.001 -0.007
child<6 (0.019) (0.030) (0.031)
Full-family sanction * -0.025 0.029 -0.007
child<6 (0.018) (0.036) (0.023)
. . . . 0.022 -0095 -0.120***
*

”“6 "m" Chm“ (0.021) (0.089) (0.025)

R-squared 0.07 0. l 7 0.16

 

 

Notes: *, **, and *** represent significance levels of 10, 5, and 1 percent. Standard errors clustered by
state are shown in parentheses. All regressions control for mother’s characteristics as listed in Table 3,
both year and state fixed effects, and their interactions with child younger than 6. N = 30,300.

118

Appendix

Figure 3.1: Distribution of Child Care Subsidy

 

 

200 400 1000 1200

 

 

 

 

600 800
Child care subsidy
v; -
Q _
g N -
1'. .-
u. .( .Ifii' git». 7.1
O i‘ ‘T" 1‘“ 7| “I: I? A i L
-300 —200 -100 0 100 200 300
Change in child care subsidy

119

Table 3.6: Federal Poverty Level and Minimum Wage Earnings (in 2007 Dollars)

Full-time earnings at state minimum

 

 

Federal poverty guideline for a wage rate

family of 2 (1 parent and 1 child) Min Max Mean
2001 13,589 7,843 15,802 12,505
2002 13,759 11,869 16,478 12,553
2003 13,655 11,604 16,111 12,349
2004 13,707 11,303 15,715 12,113
2005 13,618 10,933 16,198 12,162
2006 13,573 5,450 16,308 12,572
2007 13,690 5,300 16,300 12,852

 

120

 

Table 3.7: OLS Estimates of the Effect of Child Care Subsidy (without Other Welfare
Policies)

 

Dependent variable

 

Received child care

 

 

assistance Employed Full-time employed
(1) (2) (3)

Baseline model
Child care subsidy (in 0.004 0.003 0.011***
100) (0.003) (0.003) (0.004)
Comparing across child ages
Child care subsidy (in 0.002 0.004 0.009”
100) (0.002) (0.004) (0.004)
Child care subsidy * 0.005 —0.004 0.004
child<6 (0.007) (0.005) (0.009)

 

Notes: *, **, and **"‘ represent significance levels of 10, 5, and 1 percent. Standard errors clustered by
state are shown in parentheses. A11 regressions control for mother’s characteristics as listed in Table 3, and
both year and state fixed effects. N = 30,300.

121

 

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124