WPS5001
Policy Research Working Paper 5001
Impact Evaluation Series No. 36
Own and Sibling Effects of Conditional
Cash Transfer Programs
Theory and Evidence from Cambodia
Francisco H. G. Ferreira
Deon Filmer
Norbert Schady
The World Bank
Development Research Group
Poverty and Inequality Team
&
Human Development and Public Services Team
July 2009
Policy Research Working Paper 5001
Abstract
Conditional cash transfers have been adopted by a large for eligible children--due to all three effects--but have
number of countries in the past decade. Although an ambiguous effect on ineligible siblings. The ambiguity
the impacts of these programs have been studied arises from the interaction of a positive income effect
extensively, understanding of the economic mechanisms with a negative displacement effect. These predictions are
through which cash and conditions affect household shown to be consistent with evidence from Cambodia,
decisions remains incomplete. This paper uses evidence where the child-specific program makes modest transfers,
from a program in Cambodia, where eligibility varied conditional on school enrollment for children of middle-
substantially among siblings in the same household, to school age. Scholarship recipients were more than 20
illustrate these effects. A model of schooling decisions percentage points more likely to be enrolled in school and
highlights three different effects of a child-specific 10 percentage points less likely to work for pay. However,
conditional cash transfer: an income effect, a substitution the school enrollment and work of ineligible siblings was
effect, and a displacement effect. The model predicts that largely unaffected by the program.
such a conditional cash transfer will increase enrollment
This paper--a product of the Poverty and Inequality Team and the Human Development and Public Services Team,
Development Research Group--is part of a larger effort in the department to study the impact of social programs and their
role in promoting human development. Policy Research Working Papers are also posted on the Web at http://econ.worldbank.
org. The authors may be contacted at fferreira@worldbank.org, dfilmer@worldbank.org and nschady@worldbank.org .
The Impact Evaluation Series has been established in recognition of the importance of impact evaluation studies for World Bank operations
and for development in general. The series serves as a vehicle for the dissemination of findings of those studies. Papers in this series are part
of the Bank's Policy Research Working Paper Series. The papers carry the names of the authors and should be cited accordingly. The findings,
interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the
International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of
the World Bank or the governments they represent.
Produced by the Research Support Team
Own and Sibling Effects of Conditional Cash Transfer Programs:
Theory and Evidence from Cambodia
Francisco H. G. Ferreira
Deon Filmer
Norbert Schady
Development Research Group
The World Bank
We thank Felipe Barrera, Luis Benveniste, Eric Edmonds, Ariel Fiszbein, and Karen Macours for very helpful
comments, as well as the World Bank Education Team for Cambodia and the members of Scholarship Team of the
Royal Government of Cambodia's Ministry of Education for valuable assistance in carrying out this work. This
work benefited from funding from the World Bank's Research Support Budget (P094396) as well as the Bank-
Netherlands Partnership Program Trust Fund (TF055023). Ryan Booth provided excellent research assistance. The
findings, interpretations, and conclusions expressed in this paper are those of the authors and do not necessarily
represent the views of the World Bank, its Executive Directors, or the governments they represent.
1. Introduction
Many programs in the developing world make transfers to poor households conditional on the
school enrollment of school-aged children. These programs have been shown to increase school
attendance in a variety of settings. Frequently, impacts are concentrated on children in grades where, in
the absence of the program, school dropout is large (see Schultz 2004 on the PROGRESA program in
Mexico, and Schady and Araujo 2008 on the BDH program in Ecuador). This has led to calls for cash
transfers to be directed towards households with children in these transition grades, on the grounds that
this would be a more cost-effective way of increasing school attainment (de Janvry and Sadoulet 2006).
Such child-specific conditional transfers could potentially have important implications for the
school enrollment of ineligible siblings, but these effects are hard to sign ex ante. Depending on the
magnitude of the transfer, its income effect might lead to increased enrollment for all children in the
household, whether or not the transfer is conditioned on any action on their part. Various models of
schooling and child labor predict that greater family income during childhood increases school enrollment
and reduces the time children spend working, quite independently of any conditionality (Ben-Porath
1967; Basu and Van 1998; Baland and Robinson 2000). On the other hand, cash transfer programs
conditional on the school enrollment of one specific child might lead parents to reallocate child work
away from the recipient and to other children in the household. Evidence of this effect has been found in
some settings, including Colombia (Barrera-Osorio et al. 2008). More generally, the transfer may provide
an incentive for parents to specialize in the education of the recipient, leading to a displacement of--less
schooling for--his or her siblings.
In this paper, we assess the impact of a child-specific conditional cash transfer program on the
school enrollment and work of recipients and their ineligible siblings. For this purpose, we first construct
a simple model of child occupational choice. The main prediction of the model is that child-specific
conditional cash transfer programs will unambiguously increase school enrollment among eligible
children, but will have an ambiguous effect on ineligible siblings. The effect on eligible children reflects
mutual reinforcement between a positive income effect, which affects the entire household, and a positive
2
but child-specific substitution effect, which is brought on by the reduction in the opportunity cost of
schooling for the eligible child. The displacement effect is also positive for these children, as it refers to
situations in which they displace their siblings from school. The ambiguity of the effect on ineligible
siblings arises from the opposing (positive) income and (negative) displacement effects of the transfer on
these children.
We then take the predictions of the model to data from Cambodia, where a program known as the
CESSP Scholarship Program (CSP) makes very modest transfers, equivalent to between 2 and 3 percent
of the total expenditures of the average recipient household, conditional on school enrollment for children
of middle-school age. The results show that children who received scholarships were about 20 percentage
points more likely to be enrolled in school, and 10 percentage points less likely to work for pay. However,
the school enrollment and work of ineligible siblings was largely unaffected by the program. These results
are robust to a variety of specification checks.
These findings have important implications for the way in which we think about household
decisions regarding school enrollment and child labor, and for the design of cash transfer programs. We
highlight three. First, the very large effect of the CSP program on the behavior of recipients confirms that
scholarship and conditional cash transfer programs may be an effective way of increasing school
enrollment in low income countries (see Filmer and Schady 2008, 2009a on Cambodia; Chaudhury and
Parajuli 2008 on Pakistan). This is important because most of the evidence on these programs refers to
Latin America, where income levels are generally higher and institutions stronger than in many African
and Asian settings where such programs are now being implemented. 1
Second, and as a cautionary counterpoint, our model suggests that very narrow age ranges for
benefit eligibility could potentially lead to the unintended displacement of some poor children from
school. Although this displacement did not take place in Cambodia (where sibling enrollment was
unchanged), it is certainly a theoretical possibility, and one which appears to have been observed in
1
The literature from Latin America is extensive--see, among others, Schultz (2004) and Behrman et al. (2005) on
Mexico; Schady and Araujo (2008) on Ecuador; Attanasio et al. (2005) on Colombia; Glewwe and Olinto (2004) on
Honduras; Maluccio and Flores (2005) on Nicaragua. Fiszbein and Schady (2009) review these and other studies.
3
practice in Colombia, where child-specific CCTs increased own enrollment, but reduced sibling
enrollment. Our model allows for both the empirical results observed in Cambodia and Colombia: The net
effect on ineligible siblings depends on the relative magnitudes of the income effect of the transfer and of
its displacement effect. This depends on size of the of the income transfer, as well as on the extent to
which--in the absence of the program--eligible children would have been more, or less, likely to be
enrolled than their ineligible siblings.
Third, the model cautions against generally interpreting a comparison of program effects for
recipients and their siblings as definitive evidence about the relative size of the income and substitution
effects of the transfer. The much larger net impact on eligible children is certainly consistent with an
important role for the substitution effect, and this would confirm other findings in the literature
(Bourguignon, Ferreira and Leite 2003; Todd and Wolpin 2006; Schady and Araujo 2008; de Brauww
and Hoddinott 2009). But it can not be interpreted as identifying these effects, since there is a third
effect--namely the displacement effect--which contributes negatively to the sibling effect, and positively
to the own effect. In a context where ineligible children in transfer-receiving households are relatively
numerous, more work is needed on quantifying the displacement effect.
The rest of the paper proceeds as follows. The next section describes our simple schooling
decision model and introduces a child-specific CCT. Section 3 briefly discusses the CSP and the data we
use for the evaluation. Section 4 discusses our empirical specification. The main results are presented in
Section 5. Section 6 concludes.
2. The model
This section presents a basic model of schooling decisions, which adapts the early insights of
Ben-Porath (1967), and of a large subsequent literature, to the specific context of a multiple-children
household facing a child-specific CCT intervention. The model has two periods, and is partial equilibrium
in nature. There is a continuum of households, each consisting of a parent and two children. Parents live
only for the first period, but care about (the perfect foresight expectation of) their children's wellbeing in
4
period 2. They take all decisions in period 1 so as to maximize household welfare, which is a function of
(
the family's consumption level in period 1, and of the expected utility of both children: W c p , U 1 , U 2 . )
Following Becker (1991) and Baland and Robinson (2000), we assume that this function is additively
separable as follows: 2
W (c p , U 1 , U 2 ) = U (c p ) + [U (c1 ) + U (c 2 )] (1)
The subscripts p, 1 and 2 denote the parent(s) and each child respectively. U(.) is an individual utility
function that is common across all individuals in the household, and which satisfies the usual properties:
U ' > 0 , U ' ' < 0 , U (0) = 0 , lim c 0 U ' (c ) = and lim c U ' (c ) = 0 . Adults earn income A (from
labor and capital), which is determined exogenously to the model. A is distributed according to a
cumulative distribution function F(A), with positive mass everywhere on a non-degenerate support 0, A . ( )
This exogenous adult income is the only source of ex ante household heterogeneity in the model.
Parents use all of their endowment of time in period 1 to supply labor inelastically. They then
choose between two occupations for their children in period 1: children can either work, in which case
they are paid a wage w, or they can go to school. 3 The model assumes that there are no school fees, but
this is merely an innocuous simplifying assumption. If each child had to pay a fixed fee f to attend school,
then the total cost of schooling would be w + f instead of just the opportunity cost w, and adult disposable
income when both children are enrolled would be B = A - 2f. The remainder of the model would be
unchanged.
2
Our parental welfare function is a simple transformation of Baland and Robinson's (2000), adjusted for the fact
that parents do not consume in period 2. This eliminates the discussion of bequests and savings which, although
essential for the efficiency argument in Baland and Robinson (2000), is not important for our purposes. Our discount
parameter plays the same role as their "altruism parameter" . For reasons which will become obvious, we focus
on two (rather than n) children, but nothing of substance hinges on this, other than considerable presentational
simplicity.
3
As in Basu and Van (1998) and Baland and Robinson (2000), we abstract from the actual decision-making process
within the household. As argued by Basu and Van (1998): "[the] model does not conflict with recent evidence and
theories which ask for the rejection of the `unitary model' of the household. This is because we assume that a child's
labor supply decision is taken by a parent. [...] this decision could be different if the decision-making were shifted
to another member of household." (p. 415).
5
The choice of occupation for child i is denoted by i , which takes the value 1 if child i is sent to
school, and 0 if she is sent to work. 4 There is a positive return to schooling, so that their period 2 income
is higher if they attend school in period 1 (h), than if they do not (). There are no capital markets and
parents cannot leave financial bequests to their children, so that the only way to invest in their future is
through education.
The household's problem is then to maximize (1), by choice of 1 , 2 subject to:
c p = A + w(2 - 1 - 2 ) (2)
ci = h i + (1 - i ) , i = 1,2 (3)
i {0,1} i = 1,2 (4)
where w > 0 and h > > 0.
The discrete nature of the control variable implies that the optimal decision for each household
cannot be obtained from calculus. Instead, the utility levels arising from each possible decision must be
compared against one another. Since instantaneous utility is concave in income, these levels will depend
on the exogenous level of adult income, A. For example, households will choose to enroll both their
children if:
U ( A) + 2U (h ) U ( A + w) + [U (h ) + U ( )] (5)
They will choose to enroll one child, but not both if
U ( A + w) + [U (h ) + U ( )] > U ( A) + 2 U (h ) and (6)
U ( A + w) + [U (h ) + U ( )] U ( A + 2w) + 2U ( )
In fact, we can show that:
Proposition 1: There exist positive income levels A* and A**, A* < A**, such that:
(i) for A < A*, 1 = 2 = 0 ;
4
Although the binary nature of this decision problem simplifies the presentation, the qualitative results extend to a
version of the model in which is continuous in [0,1], so that children may divide their time between school and
work. This extension, which also allows for child leisure, is not presented here to economize on space, but it is
available from the authors on request.
6
(ii) for A* A < A**, i = 0, j = 1 ; i j
(iii) for A** A, 1 = 2 = 1 .
Proof: See Appendix 1.
Proposition 1 states that when households are identical in all dimensions other than adult income,
and school enrollment has an opportunity cost (given by the forgone earnings of children in period 1),
then enrollment decisions vary monotonically with family income. Above a certain adult income level
A**, all children are enrolled in school (and none work). Below a lower threshold A*, no children are
enrolled (and all work). Between the two thresholds, households can afford to (and do) enroll one child,
but not the other. In that income range, and under our simplifying assumption that siblings are identical
(in schooling ability, in labor productivity and in how much their parents value them), the decision of
which child to enroll from each household is random, with child i being sent to school with probability i
( 1 + 2 = 1 ). 5
Figure 1, which illustrates the proof of Proposition 1, shows that A* marks the income level at
which the discounted gain in expected child utility from enrollment ( [U (h ) - U ( )] ) equates the
opportunity cost in first-period consumption from forgoing the earnings of a first child
( U ( A + 2 w) - U ( A + w) ). Point A** marks the corresponding income level for the second child, and it is
clear that the existence of the intermediate range depends on utility being strictly concave in first period
consumption.
There are clear parallels to the previous literature. This strong negative relationship between
household income and child labor is reminiscent of Basu and Van's (1998) result that child labor arises
only from households in poverty, with no need for a strong "luxury axiom". As in Baland and Robinson
5
In a richer model, children might be allowed to differ in school ability, work productivity or parental preference.
Such differences would alter the model in two ways. First, for households with A* A < A**, child heterogeneity
would alter the pre-transfer decision of which children to enroll. This change can be accommodated by our set up
with i j . More importantly, however, child heterogeneity would lead to a finite elasticity for the displacement
of ineligible by eligible children once the transfer is introduced. This extension is left for future work, and we note
only that the magnitude of the displacement effect we consider here is likely to be an upper-bound, since it assumes
perfect substitutability across children.
7
(2000), the result is driven by missing capital markets: if families could borrow in period 1 against the
child's income in period 2 then, for sufficiently large returns to education (i.e. for a sufficiently large
value of h - ), child labor could be eradicated. Without that ability to borrow, poor households, for
whom the marginal value of period 1 consumption is very high, use child-labor as an (inferior) alternative
consumption-smoothing mechanism.
In this setting, a conditional cash transfer is a monetary payment in period 1, which is made if
and only if a child is enrolled in school. Since we are interested in a situation where some children are
eligible for the transfer but others are not, even within the same household, assume (without loss of
generality) that only child 1 is eligible for the transfer. This policy leaves the household's problem
unchanged, except for equation (2), which is replaced by:
c p = A + w(2 - 1 - 2 ) + 1 (2')
The effect of this policy on the household's decisions is twofold. First, it changes the adult income
thresholds at which first one, and then both children are enrolled. Parents will now enroll both children if:
U ( A + ) + 2U (h ) U ( A + w + ) + [U (h ) + U ( )] (7)
The income level which satisfies (7) as an equality is A** . It is easy to see, once again from the concavity
of the utility function, that A** < A * * . Parents will enroll one child (but not both), if (7) does not hold
and:
U ( A + w + ) + [U (h ) + U ( )] U ( A + 2w) + 2U ( ) (8)
A* , which solves (8) as an equality, is less than A**.
The second change in household behavior is that, under the maintained assumption that siblings
are identical, the choice of which child to enroll for those parents who enroll a single child is now no
longer random. They all choose to enroll child 1, who is eligible for the transfer, which leads to the
potential displacement effect.
8
Adult labor continues to be supplied inelastically; Appendix 2 shows that this is a reasonable
approximation for Cambodia.
Figure 2 illustrates the changes brought about by the conditional cash transfer. The two-child
enrollment threshold falls (from A** to A** ) because of a pure income effect: the value of the transfer is
added to both sides of inequality (7), and the dashed curve U ( A + w + ) - U ( A + ) lies below the
original curve U ( A + w) - U ( A) simply because that difference declines with income.
The reduction in the one-child enrollment threshold (from A* to A*), on the other hand, arises
from both an income and a substitution effect. The value of the transfer is added only to the left-hand-side
of inequality (8), so that the dashed curve U ( A + 2 w) - U ( A + w + ) lies below the original curve
U ( A + 2 w) - U ( A + w) because of a full "price effect", comprising both an income and substitution
effect.
This allows us to state:
Proposition 2: The introduction of a child-specific conditional cash transfer that alters the household
budget constraint from (2) to (2') will:
(i) unambiguously increase enrollment of the eligible children (child 1);
(ii) have an ambiguous effect on the enrollment of the ineligible children (child 2).
Proof of Proposition 2.
Denote by i the proportion of children of type i (i = 1,2) enrolled by families with a single child
attending school prior to the introduction of the transfer. If children of types 1 and 2 were enrolled with
equal probability by families with income in the interval (A*, A**), then 1 = 2 = 0.5 . Then pre-
transfer enrollment for child i was given by:
Ei = 1 - F ( A * *) + i [F ( A * *) - F ( A *)] i = 1, 2 (9)
Post-transfer enrollment is different for the two types of children, and given by:
9
( )
E1 = 1 - F A* (10)
E2 = 1 - F (A )
**
(10')
Changes in enrollment are obtained from subtracting (9) from (10):
( )
E1 = (1 - 1 )F ( A * *) + 1 F ( A *) - F A* > 0 (11)
( ) ( )
where the inequality arises from the fact that F ( A * *) > F A* and F ( A *) > F A* . This proves (i).
( )
E 2 = (1 - 2 )F ( A * *) + 2 F ( A *) - F A** (12)
Since A** may be greater than A* (and indeed will be greater for < w), the sign of E2 may depend on
the specific value of 2 (0,1) . This proves (ii).
While the model predicts an ambiguous impact of the child-specific CCT on siblings, it does
allow us to go one step further and assess the likely relative size of the impacts on recipients and their
siblings. Subtracting (10) from (9) is a comparison of the changes in enrollment for eligible and non-
eligible children. E1 > E 2 so long as
( ) ( )
F A** - F A* > ( 1 - 2 )[F ( A * *) - F ( A *)] (13)
A corollary of Proposition 2, then, is that 1 2 is a sufficient (but not necessary) condition for
E1 > E 2 . In other words, if eligible children were initially either equally or less likely to be enrolled
than ineligible children, then their enrollment will increase by more as a result of the transfer. The
necessary condition, which is given by (11) is evidently much weaker: if the measure of the population
between A* and A** is not very different from the mass between A* and A** , then one would need a
pre-transfer situation in which almost all eligible children were already enrolled (1 1), while almost
all ineligible children were not (2 0). It is hard to conceive that a CCT would be targeted to type-1
children if this were the case. We thus say that (13) "generally" holds, and that the enrollment effect of
CCTs on eligible children is in those circumstances larger than the enrollment effect on ineligible
siblings.
10
In sum, our simple model of schooling decisions for a multi-child household predicts that a child-
specific conditional cash transfer will lead to increased enrollment for eligible children. This increase
reflects the combination of effects. First, there is a displacement effect among those households that only
enroll one child: they tend to replace their ineligible children with their eligible siblings in school.
Second, some households that would not send any children to school in the absence of the program are
now compelled to send an (eligible) child to school, due both to a substitution effect (the opportunity cost
of that decision has fallen from w to w ) and to an income effect (an increase in unearned period 1
income reduces the utility loss from forgoing that opportunity cost).
The effect on the enrollment of ineligible children is ambiguous. The displacement effect works
against them, with families that send a single child to school shifting away from them towards their
eligible children. Furthermore, they do not benefit from a substitution effect, since the opportunity cost of
their going to school remains equal to w. However, some ineligible children can benefit from an income
effect. Those are children in households whose income levels in the absence of the transfer were just
insufficient to enroll both children but who, given the extra income from the transfer, are now willing to
forgo the child earnings from their second child as well. (These are households with exogenous incomes
between A** and A** in Figure 2.) This is a pure income effect, since they receive no additional transfer
for this added enrollment.
3. Program and data 6
Cambodia has had programs that offer "scholarships" to poor children making the transition from
primary to lower secondary school for a number of years. These programs have operated in some regions
of the country and not others, and have been funded from a variety of sources, including government
budgets, loans from multilateral and bilateral donor agencies, and NGOs. One of the programs that
predated the CSP, known as the Japan Fund for Poverty Reduction (JFPR) scholarship program, was
6
Sections 3 and 4 draw from Filmer and Schady (2009b).
11
targeted at girls (and children from ethnic minorities) making the transition from primary school to lower
secondary school. Filmer and Schady (2008) evaluate the program and conclude that, despite the small
amount of the transfer, which (like the CSP) accounted for only 2-3 percent of the total consumption of
the median recipient household, the JFPR increased enrollment rates by almost 30 percentage points.
Program effects were particularly large among girls in the poorest households.
In the time period we study, the CSP operated in 100 of the approximately 800 middle schools in
Cambodia. These schools were selected on the basis of administrative data which indicated that poverty
rates in the areas served by these schools were high and, by implication, secondary school enrollment
rates low. In addition, there was a requirement that none of the selected schools participate in other
scholarship programs, including the JFPR.
The selection of CSP recipients within eligible schools was done in three stages. First, using
administrative data from the 100 CSP schools, program officials identified all of the primary "feeder"
schools for every CSP school. (A primary school was designated a feeder school if it had sent graduating
students to a given CSP school in recent years.)
Second, within feeder schools all 6th graders were asked to complete a CSP "application" form--
regardless of whether these students or their parents had previously expressed an interest in attending
secondary school. The application form consisted of 26 questions about characteristics that were highly
correlated with the probability of school dropout, as indicated by analysis of a recent nationwide
household survey; the questions were also reasonably easy for students of this age to answer, and for
peers and teachers to validate. In practice, the form elicited information on household size and
composition, parental education, the characteristics of the home (the material of roof and floors),
availability of a toilet, running water, and electricity, and ownership of a number of household durables.
Forms were filled out in school, on a single day. Students and parents were not told beforehand of the
content of the forms, nor were they ever told the scoring formula--both decisions designed to minimize
the possibility of strategic responses; for example, by a student seeking to maximize her chances of
receiving the award. Once completed, forms were collected by head-teachers, and sent to the capital,
12
Phnom Penh. There, a firm contracted for this purpose "scored" them, using the responses and the set of
weights that reflected how well each characteristic predicted the likelihood of school dropout in the
nationwide household survey. The formula used was the same for every school and, once calculated, the
scores could not be revised.7
Finally, within every CSP school, all applicants were ranked by the score, regardless of which
feeder school they came from. In "large" CSP schools, with total enrollment above 200, 50 students with
the lowest value of the score were then offered a scholarship for 7th, 8th, and 9th grade; in "small" CSP
schools, with total enrollment below 200 students, 30 students with the lowest value of the score were
offered the scholarship. 8 In total, just over 3800 scholarships were offered in the year of the program we
study. 9 The list of students offered scholarships was then posted in each CSP school, as well as in the
corresponding feeder schools.
Once children had been selected to receive a CSP scholarship, their families received the cash
award three times a year. Payments were made at widely attended school ceremonies, with the school
principal publicly handing over the cash to parents. The majority of participants at these school
ceremonies were CSP recipients. During the ceremonies, principals stressed the importance of secondary
school education, and the responsibilities that parents had to ensure that their children were enrolled in
school, attended regularly, and were successful students. Also, parents were told that they were meant to
spend the CSP award on the schooling of the selected children. Although no attempt was made to monitor
7
Scholarship recipients and their scores were posted at feeder schools and at CSP schools. There was a complaint
mechanism whereby community members could appeal the decisions made on the basis of the score--either because
they believed that an applicant had mis-represented their characteristics on the form, or because they believed an
applicant was poorer (or less poor) than indicated by the score. In practice, however, less than 1 percent of
applicants appealed the decisions, and the recipient status of even fewer was revised as a result of a complaint.
8
In practice, within every large school, the 25 students with the lowest dropout score were offered a scholarship of
$60, and the 25 students with the next lowest scores were offered a scholarship of $45; in small schools, the
comparable numbers were 15 students with scholarships of $60, and 15 with scholarships of $45. We do not focus
on this distinction in this paper. Rather, we compare applicants who were offered a scholarship, regardless of the
amount, with others that were not. Because the identification strategy is regression-discontinuity, we are implicitly
comparing applicants who were offered a $45 scholarship, with those who were offered no scholarship at all.
Students who were offered a $60 scholarship help estimate the control function that relates enrollment to the dropout
score.
9
Occasionally, there were tied scores at the cut-off. In these cases, all applicants with the tied score at the cut-off
were offered the scholarships.
13
household expenditures, CSP recipients may have responded powerfully to these messages, perhaps
especially so given a tradition of deference to authority in Cambodia.
We analyze the impact of the program among the first cohort of eligible children. These children
filled out the application forms in May 2005, and the list of scholarship recipients was posted in
November 2005. We use data on children at two points in time. First, we have access to the composite
dropout score, as well as the individual characteristics that make up the score for all 26,537 scholarship
applicants. Second, we fielded a household survey of 3453 randomly selected applicants and their
families in five provinces: Battambang, Kampong Thom, Kratie, Prey Veng, and Takeo.10 The household
survey was collected between October and December of 2006, approximately 18 months after children
filled out the application forms. Since application forms were filled out at the end of 6th grade, estimates
of program effects on the school enrollment of applicants based on the household survey refer to the
beginning of 8th grade. 11
Table 1 summarizes the characteristics of CSP recipients and non-recipients, as reported on their
application forms--separately for all applicants (left-hand panel) and applicants within ten ranks of the
cut-off of the score (right-hand panel). The first four columns of each panel show that, as expected,
recipients are generally poorer than non-recipients. For example, in the full sample, CSP recipients are
less likely to own a bicycle (54 percent of recipients own one versus 76 percent of non-recipients); less
likely to own a radio (25 versus 39 percent); and less likely to live in a dwelling whose roof is made of
solid materials such as tiles, cement, concrete or iron (44 versus 65 percent). The differences between
recipients and non-recipients are smaller when we limit the sample to children whose value of the score is
closer to the cut-off.
10
The sample was based on randomly selected schools in these five provinces. The survey was limited to applicants
ranked no more than 35 places above the cutoff in these schools. This restriction was imposed to maximize the
number of schools, while maintaining the density of observations "around" the cut-off--an important consideration
when estimating program effects based on regression-discontinuity, as discussed below.
11
We also have access to a third set of data. These come from four unannounced visits to the 100 CSP schools (in
February, April, and June 2006, and in June 2007) in which the physical attendance of applicants was verified.
These allow us to validate our schooling impacts on recipients (as we discuss below), but do not allow an analysis of
labor impacts nor sibling effects.
14
The final two columns in each panel of Table 1 report the coefficient and p-value in a regression
of each characteristic on the application form on a quartic in the composite score, school fixed effects,
and dummies for the age of the child and her birth order. This corresponds to our basic estimation
specification, discussed in more detail below, and is a standard check on the validity of the regression
discontinuity (RD) specification (Imbens and Lemieux 2008). This specification check suggests that
differences between recipients and non-recipients are unlikely to be an important source of bias to our
estimates of program impact. In the full sample, the coefficients on only two characteristics are
significant--the probability that a child is a boy, and the fraction of households with floors made of wood
planks or bamboo. We estimate the impact of the CSP program separately for boys and girls throughout,
which removes any possible bias associated with differences in the gender composition of recipients and
non-recipients. The difference in the proportion of households with floors made up of wood planks or
bamboo is not significant when the sample is limited to children whose score places them within ten
points of the cut-off. As a robustness check on our estimates of CSP program effects, we therefore also
present results for this smaller sample.
In order to place our results in context, Table 2 summarizes enrollment and work outcomes for
children in the control group, separately for applicants and their siblings, and by gender. We consider six
different outcome variables. The first three are the probability of enrollment, working for pay, and
working without pay. These are binary indicator variables--for example, enrollment takes on the value of
one if a child is enrolled in school, and zero otherwise. The remaining variables correspond to the number
of hours an applicant or their sibling attended school, worked for pay, and worked without pay,
conditional on the relevant binary variable taking on a value of one. (For example, hours in school refer
only to children who are enrolled in school.) The measures of hours of school attendance and work refer
to the last seven days. 12
12
The definitions of these variables follow the questionnaire on which the data are based. Work for pay is defined as
"work for pay on a farm, public or private sector, or in a business belonging to someone else." Work for no pay is
defined as "work for no pay on a farm, private or public sector, own account or in a business belonging to yourself
or someone else in your household."
15
The table shows that enrollment of boys is higher than that of girls: in this sample of applicants
who were not offered a scholarship 63 percent of boys and 54 percent of girls are enrolled. Among their
siblings, who are on average younger, overall school enrollment is higher--86 percent for boys and 80
percent for girls. Applicants who are enrolled in school attend, on average, for about 26 hours per week,
and their siblings attend for approximately 21 hours.
About 31 percent of applicant boys in the control group worked for pay, compared to 37 percent
of girls: Among those who work for pay, average hours are 24 for boys and 28 for girls. Siblings are
much less likely to work for pay--9 percent of boys and 17 percent work of girls work. Work for pay
among children in this age group is concentrated in the farm sector and construction for boys, and in the
farm sector and garment industry for girls.13
Work without pay is much more widespread among applicants and their siblings: 64 percent of
applicant boys and 51 percent of applicant girls work without pay. On average, these children work for
about 19 hours. Among siblings, the incidence of work for pay is once again lower--52 percent among
boys, and 47 percent among girls.
The last two columns of the table focus on patterns of work among applicants' parents. Many
more adults work in the no-pay sector than in the for-pay sector, a pattern that is apparent for both men
and women. Work hours are approximately 30 hours per week in the for-pay sector, and 32 to 36 hours in
the no-pay sector.
4. Identification strategy
The basic identification strategy we use in this paper is based on regression discontinuity (RD).
The regressions we estimate take the following form:
(14) Yihs = s + f(Sh) + Xi + (R*Male)1 + (R*Female)2 + (R*S*Male)3 + (R*S*Female)4 + ihs
13
Our survey did not collect information on what work for pay children are engaged in, so we make use of a recent
nationwide household survey, the 2004 Cambodia Socio-Economic Survey (CSES). We limit the sample in the
CSES to rural areas, which most closely corresponds to the catchment areas of the CSP schools. In rural areas, 35
percent of boys age 10-18 who work for pay are farm workers, and another 26 percent work in construction; among
girls, 35 percent of those who work for pay are farm workers, and 27 percent work in the garment industry.
16
where Yihs is an outcome variable, for example, the probability that child i in household h and CSP school
s is enrolled in school; s is a set of CSP school fixed effects; f(Sh) is the control function, a flexible
parametrization of the dropout score. In our main results, we use a quartic in the score and allow the
function to differ for males and females; we also test for the robustness of the results to this choice of
functional form. Xi includes a set of single year age dummies and a set of birth order dummies. Xi also
includes dummy for males, a dummy for siblings, and the interaction between siblings and males. The
variables R*Male (R*Female) take on the value of one if the observation is a male (female) applicant who
was offered a scholarship; the variables R*S*Male (R*S*Female) take on the value of one for male
(female) siblings of applicants who were offered a scholarship; and ihs is the regression error term. All
regressions are limited to school-aged children, ages 7-18. Standard errors account for clustering at the
level of the primary feeder school.
In this set-up, the parameters 1 and 2 are estimates of the program impact on male and female
recipients, respectively, while the parameters 3 and 4 are estimates of the program impact on the male
and female siblings of recipients, respectively. Note that because we include the main effects for boys and
siblings in the vector Xi, as well as the interaction terms between them, we are comparing treated
applicants to control applicants (and not to their siblings), and treated siblings to control siblings (and not
to applicants).
Three things are worth noting about this specification. First, because the score perfectly predicts
whether or not an applicant is offered a scholarship, this is a case of sharp (as opposed to fuzzy) RD.
Second, because we focus on the impact of being offered a scholarship, rather than that of actually taking
up a scholarship, these are Intent-to-Treat (ITT) estimates of program impact. Third, as with every
approach based on RD, the estimated effect is "local". Specifically, it is an estimate of the impact of the
scholarship program around the cut-off. However, where the cut-off falls in terms of the dropout score
varies from school to school. This is because the number of students offered the scholarship was the same
in every large and small CSP school, respectively, but both the number of 6th graders and the distribution
17
of the underlying characteristics that make up the dropout score varied. 14 In practice, the value of the cut-
off varies from a score of 21 to 40 in the schools attended by the study sample, with the median at 28. The
estimates of are therefore weighted averages of the impacts for these different cut-off values.
For the three indicator variables (the probability of enrollment, of working for pay, and working
without pay) the models are estimated by OLS. For the other variables, the hours spent in each of these
activities in the past 7 days, we present results both from OLS regressions and the marginal effects from
Tobit specifications; the latter take account of the fact that the variables are censored, with a substantial
fraction of the sample reporting zero.15
5. Results
5.1 Main results
Before turning to the estimates of equation (14) we motivate our results by showing outcomes as
a function of the ranking based on the dropout score, relative to the cut-off. We do this by plotting
average outcomes at each value of the relative ranking, and overlaying a quartic in the score.16,17 Figure 3
has six panels, corresponding to enrollment, work for pay, work without pay for applicants and their
siblings. In each case, distinct "jumps" at the cut-off would suggest that the program affected behavior.
For applicants, panel A suggests that the program had large effects on enrollment, approximately
20 percentage points; panel B suggests that the probability of work for pay dropped; and panel C suggests
14
All else being equal, in CSP schools that received more applications, and in those in which children have
characteristics that make it more likely they will drop out, a child with a high dropout score is more likely to be
turned down for a scholarship than a similar child applying to a school that receives fewer applications or serves a
population with a lower average dropout score.
15
See Black, Galdo and Smith (2007) for an application of the Tobit model in an RD framework.
16
Because the cut-off falls at different values of the underlying score in different schools, depending on the number
of applications, the mean characteristics of applicants, and whether a school was defined as "large" or "small", it is
not informative to graph outcomes as a function of the score. Rather, for these figures we redefine an applicant's
score in terms of the distance to the school-specific cut-off, so that (for example), a value of -1 represents the "next-
to-last" applicant to be offered a scholarship within a school, 0 the "last", and a value of +1 represents the "first"
applicant within a school who was turned down. The figures then graph outcomes as a function of this relative rank.
17
These parametric regressions include a quartic in the relative rank, but not the vector of school fixed effects or
child characteristics. Note that these differ slightly from the models estimated below which control for the composite
score, CSP school fixed effects, and age and birth order dummies. We note that using locally-weighted least squares
regressions (as in Fan and Gijbels 1996) instead of a quartic produces almost identical results.
18
that the program led to a small increase in the likelihood that children engaged in unpaid work. For
siblings, panels A and B suggest little relationship between scholarships and enrollment or work for pay;
panel C suggests a small increase in work without pay. Figure 1 is thus consistent with the CSP program
having had a large effect on the schooling of children who were offered scholarships, but little or no
effect on their siblings.
The results of parametric estimates of program impact, described in equation (1) above, are
reported in Table 3. For each outcome, we show estimates of program impact on males and female
recipients, as well as on male and female siblings. We also test for differences in the recipient effects by
gender (1 =2), in the sibling effects by gender (3 =4) and whether the gender-specific recipient and
sibling effects are the same [(1 =3), and (2 =4)].
The first two rows of the table confirm that the program had large effects on recipients. School
enrollment increased dramatically--by 22 percentage points for boys and 20 percentage points for girls.
This increase came hand in hand with a sharp reduction in the probability that CSP recipients work for
pay--of 12 percentage points in the case of boys, and 9 percentage points in the case of girls. Finally,
applicants also more likely to work without pay, a result that is significant for girls. Paid work may be
more difficult to combine with schooling than unpaid work, because paid work generally involves less
flexible hours and a greater intensity of work (as suggested by Edmonds 2007; Edmonds and Schady
2008). The results in Table 3 are strongly consistent with this pattern.
Before discussing the effects on siblings, we consider how the CSP program affected the hours
spent on each of these activities. These results are presented in Table 4. The left-hand panel of the table
presents the marginal effects from Tobit regressions, and the right-hand panel presents corresponding
results estimated by OLS. The coefficients on hours of schooling suggest that recipients spent 6-8 more
hours in school than non-recipients. The reduction in hours worked for pay is smaller--between 1 and 3
hours. Note that the estimated effects on hours worked without pay are negative--ranging from a
19
reduction in 30 minutes to a reduction of almost an hour and three quarters. So while the program effect
on the incidence of work without pay is positive (Table 3), recipients worked fewer hours (Table 4). 18
We next turn to a discussion of CSP program effects on the siblings of applicants, focusing on
both changes in participation (in Table 3) and hours (Table 4). Table 3 suggests that siblings of CSP
recipients increased the likelihood of work without pay by between 4 and 7 percentage points. However,
Table 4 shows that the implied change in hours is very small, and is not significant. Both tables also make
clear that the school enrollment choices of siblings were unaffected by the program.
5.2 Robustness checks
We conducted a large number of robustness checks to our main results. These include
specifications that limit the sample to children with a score that places them within 10 ranks of the school-
specific cut-off; specifications that allow for school-specific control functions (in addition to the school-
specific intercepts); specifications in which the control function is defined in terms of an applicant's
ranking relative to the school-specific cut-off (as in Figure 3), rather than in terms of the score; and
specifications that separately consider program effects on older and younger siblings. None of these
changes has a qualitatively important effect on our basic results.
A. Sample restricted to households within 10 ranks of cut-off: A standard check on the RD
specification involves testing whether the estimated coefficients are robust to limiting the sample to
observations that are "close" to the cut-off. We do this by restricting the sample to children in households
with a score that places them no further than 10 ranks from the school-specific cut-off. This comes at a
cost--our sample is reduced by almost two-thirds (from 8182 observations to 2920).
The results from this robustness check are reported in the left-hand panel of Table 5. In terms of
work, the coefficients in this smaller sample tend to be somewhat larger for boys. For example, among
applicants, we estimate a reduction in work for pay of 18 (rather than 12) percentage points; among male
siblings, we estimate an increase in work without pay of 7 (rather than 5) percentage points. Among girls,
18
We also carried out this analysis for an additional activity; household chores. We found small and statistically
insignificant program effects on time spent in household chores. These results are available from the authors on
request.
20
the only notable change is that the coefficient on work for pay for applicants is reduced substantially,
from 9 to 5 percentage points, and is no longer significant. In terms of schooling, the results for the
smaller sample are extremely close to those estimated for the full sample of children. Because the results
for the smaller sample are very similar to those that use the full sample of children, we conclude that our
main set of results is not driven by possible biases introduced by using observations that are "far" from
the cut-off.
B. School-specific control function: Although our basic specification allows for school-specific
intercepts, it imposes a common control function across schools. This assumes that a given change in
household socioeconomic status (as measured by the composite score) is associated with an increase in
the probability of enrollment or work of the same magnitude across all schools. Conceivably, such an
assumption of equal control functions may not do justice to the data. For example, there may be
differences in school quality which affect not only whether school enrollment is higher in some schools
than in others at all levels of socioeconomic status (a difference in intercepts across schools), but also the
gradients between socioeconomic status and enrollment (a difference in slopes across schools).
The right-hand side of Table 5 reports results from specifications that allow for school-specific
quartic trends and intercepts. This places large demands on the data--for each school, there are two
intercepts (for boys and girls), and eight polynomials in the score (quartics for boys and girls), for a total
of 570 terms. The right-hand panel of Table 5 shows, however, that the results from this more flexible
formulation are very close to those that impose a common control function. For example, in this
specification the CSP program effect on the probability that applicant boys are enrolled in school implies
an increase of 19 percentage points (compared to 22 points in the specification that imposes a common
control function), while that for girls implies an increase of 21 percentage points (compared to 20 points);
in terms of work for pay, the coefficients in 5 imply a reduction of 12 percentage points for boys, and 7
points for girls, compared to 12 percentage for boys and 9 points for girls in Table 3. Sibling effects
remain small and insignificant. It does not appear that the assumption of a common control function
across schools introduces substantial biases into our estimates of the impact of the CSP program.
21
C. Defining control function in terms of ranking, rather than the score: In our main set of results, the
control function is defined in terms of the score on the application form, rather than in terms of an
applicant's ranking relative to the school-specific cut-off. In principle, this could introduce biases as
recipients in some schools are compared to non-recipients with the same score in a different school.
(Although one would expect the potential biases to be small, especially in specifications that include
school-specific intercepts and slopes.) An alternative is to define the control function in terms of an
applicant's ranking relative to the school-specific cut-off. Table 6 reports the results from specifications
that are based on an applicant's rank, with a common control function (left-had panel) and school-specific
control functions (right-hand panel). In these specifications, the impact of the program on school
enrollment among applicants is a little smaller--about 18 (rather than 21) percentage points. In terms of
work, the impacts among boys appear to be somewhat larger than those in our main set of results--for
example, in the specification that allows for school-specific control functions the impact on work for pay
is 14 (rather than 12) percentage points; for girls, the estimated effects are somewhat smaller in terms of
the reduction in work for pay (6, rather than 9 percentage points), but larger in terms of the increase in
work without pay (14, rather than 7 percentage points). Among siblings, the impacts are again estimated
to be insignificant. One coefficient emerges as significant in the single control function specification:
male siblings who are recipients increase their work without pay. However, given that this result does not
feature in any other specifications, we do not think that it undermines the overall finding of lack of impact
on siblings. In general, therefore, the patterns of results in specifications that are based on rank are
similar to those that are based on an applicant's score.
D. Sibling-effects differentiated by relative age: First-born, or earlier-born, siblings have typically
been found to be less likely to attend school. 19 We investigate the extent to which our results could mask
heterogeneity by the relative age of siblings. In order to isolate the issue of relative age, we re-estimate
our basic model but now allow the impacts to differ by whether a sibling is younger or older than the
19
This has been documented in settings as diverse as Brazil (Emerson and Souza 2008), Nepal (Edmonds 2006), and
Taiwan (Parish and Willis 1993). Edmonds (2007) provides a thoughtful review.
22
applicant. (We do not differentiate by gender to keep sample sizes reasonable; however, results that
disaggregate by the gender of both the applicant and her sibling are similar to those we report, but
substantially less precise.) Table 7 shows that our results are not an artifact of aggregation: sibling effects
are not significantly (or substantively) different depending on the relative age of the sibling. 20
E. School visits: A final possible concern is the possibility of systematic reporting biases in our
measure of school enrollment based on household survey data. Conceivably, parents of scholarship
recipients could be more likely to lie to enumerators about school enrollment than those of non-recipients
(although it is less clear why they would lie about the school enrollment and work status of ineligible
siblings). As we report elsewhere, however, results from an analysis of data on directly observed school
attendance from four unannounced school visits are very similar to those that use the household survey
(Filmer and Schady 2009c). 21
5.3. Magnitude of program effects
The CSP program effects on the enrollment of eligible children are large. One way of placing the
magnitude of the effects in context is by calculating the elasticity of enrollment with respect to cost. To
do this, we calculated the total (direct and indirect) cost of schooling for children affected by the CSP
program, using data we collected in the survey, and limiting the sample to children who applied for a
scholarship but did not receive one.
The direct cost is given by the sum of various school fees, including annual fees (which include
exam fees, various "allowances" and fees for various school events and ceremonies); fees incurred at the
beginning of the school year (including registration fees, uniforms, books, and school material); and daily
20
We also explored whether restricting the analysis to siblings who are close in age to the applicant alters our
findings. For this purpose, we estimated our basic model, but restricted the sample to children (both applicants and
siblings) ages 14 to 18. Results from these estimates are very similar to those we report in the paper--that is, strong
own effects on schooling and work for pay but small and insignificant impacts on siblings. Finally, we restricted the
sample to male applicants only and analyzed the effect on brothers, and to female applicants only and analyzed the
effects on sisters--on the grounds that same-sex siblings might be closer substitutes for each other. As with the age
restriction, we do not find that restricting the sample in these ways changes our findings. These results are not
included in the paper but are available from the authors upon request.
21
The impact of being offered a scholarship on physically verified attendance is equal to 25 percentage points when
pooling across all four visits (February/March 2006; April/May 2006; June 2006; June 2007), and equal to 20
percentage points when restricting the analysis to June 2007 when the applicants would have been in 8th grade, if
they did not repeat school grades.
23
expenditures (including snacks, extra classes, bicycle parking, lesson copies and other daily expenses).
The sum of these expenses is US $44 per year per child, on average; of these, the bulk is made up of fees
incurred at the beginning of the school year (34 percent of the total), and daily expenditures (63 percent of
the total), while other annual fees are a very small amount (2 percent of the total). The indirect cost of the
CSP is given by the foregone earnings. In Table 4 above, and focusing on the Tobit marginal effects, we
show that the average recipient reduced work for pay by approximately 1.2 hours per week; separate
calculations using the survey data show that the mean hourly wage in the for-pay sector for applicant
children who did not receive scholarships is US $0.38. Assuming that the school year has 8 months, this
amounts to $14 of foregone earnings per year. Total costs (including direct and opportunity costs) are
therefore $58, while the transfer is $45. The CSP program represented a 78 percent (45/58) reduction in
costs. This, in turn, resulted in an increase in school enrollment of approximately 21 percentage points,
from a baseline value of approximately 55 percent, for an increase in enrollment of 37 percent. The
elasticity of enrollment with respect to cost is therefore 0.48 (37/78).22 (If we include the reduction in
hours worked without pay, which is not significant, and value it at the wage paid to children working for
pay, the elasticity is similar, 0.51.) Although we are not aware of estimates from other settings we could
use for comparison, this appears to be a reasonable value for this elasticity.
6. Discussion and conclusion
Cash transfer programs, both conditional and unconditional, have become very popular in the
developing world. In many countries, they have become the largest social assistance program, covering
millions of households (as is the case in Brazil, Mexico, Ecuador, and South Africa). Many of these
programs also seek to increase the educational attainment of children. However, because enrollment rates
are already very high at some school grades, some analysts have suggested that cash transfers (in
particular, those which are conditioned on school enrollment) could be made more efficient if they were
22
These calculations are weighted averages of the means and impacts for boys and girls, respectively. Similar
calculations using the OLS regression coefficients rather than the Tobit marginal effects yield an elasticity of 0.69,
which is larger because of the larger estimated effect on hours worked for pay in the OLS specifications.
24
narrowly targeted at child ages and grades where, in the absence of the program, dropout rates are high
(de Janvry and Sadoulet 2006).
In this paper, we construct a simple model of schooling decisions and how these respond to a
child-specific CCT. We show that such a program will unambiguously increase school enrollment among
eligible children, but will have an ambiguous effect on the school enrollment of their ineligible siblings.
We then take the predictions of the model to data from a child-specific CCT in Cambodia. This analysis
shows that the program significantly increased the school enrollment of eligible children, but left
schooling outcomes for their siblings unaffected.
However, this need not have been so. Barrera-Osorio et al. (2008) analyze a program in Bogotá,
Colombia. This program makes reasonably large transfers, equivalent to about 8 percent of expenditures
for the median recipient household, conditional on the school enrollment of specific children selected for
the program. 23 Barrera-Osorio et al. compare families in which two, one, or no children were selected into
the program. They conclude that the program positively affected the school enrollment of recipients, but
that this came, in part, at the expense of their siblings, who were more likely to drop out of school and
enter the labor market. Similarly, Manacorda (2006) uses historical data from the United States to show
that minimum working age laws that enabled a child of a particular age to join the labor market legally
led to a reduction in their siblings' labor participation and an increase in their siblings' school
participation.
Our simple model of two-child households can account for the results for Cambodia, Colombia,
and the early-twentieth century United States. The model suggests that households will fall into one of
three types. First, "poor" households who would send neither child to school in the absence of the
program. If these households take up the program, they will enroll the eligible child, and perhaps the
ineligible child if the transfer is large enough. Second, "middle-income" households who would send only
one child to school in the absence of the program. If these households take up the program, they will
23
The amount of the transfer and its value as a share of expenditures for the average recipient household are not
reported in the paper. We are grateful to Felipe Barrera for providing us with this detail.
25
ensure that the eligible child attends school, but this could come hand in hand with a displacement effect
on their ineligible sibling. Third, "wealthier" households who would send both children to school, even
without the program. We would expect no impact on enrollment in this case.
In any given setting there will presumably be some households of all three types. The overall
impact of the program therefore represents the average across types--and will be weighted by the
population share of each type. The case of Colombia (Barrera-Osorio et al. 2008) suggests a situation
dominated by the second type of household--the direct impact on recipients was accompanied by a
reduction in schooling among their siblings; the results reported by Manacorda (2006) for the early-
twentieth century United States are also consistent with this. In Cambodia, however, we find no evidence
of such spillovers to siblings--suggesting a situation in which most households are of the first type.
More generally, our results suggest that it is premature to conclude that cash transfer programs
that are directed at individual children will always affect siblings (positively or negatively). Rather, these
spillover effects are likely to depend on the details of the program, the age- grade-, and gender-specific
patterns of school enrollment, and the opportunities available to children outside school. Understanding
these differences across settings and programs should be a priority for future research.
26
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1920 America." American Economic Review 96(5):1788-1800.
Parish, W, and R. Willis. 1993. "Daughters, education, and family budgets: Taiwan experiences." Journal
of Human Resources 28(4): 862898.
Schady, N. and M. C. Araujo. 2008. "Cash Transfers, Conditions, and School Enrollment , and Child
Work: Evidence from a Randomized Experiment in Ecuador." Economía 8(2): 43-70.
Schultz, T. P. 2004. "School Subsidies for the Poor: Evaluating the Mexican Progresa Poverty Program."
Journal of Development Economics 74(1): 199-250.
Todd, P., and K. Wolpin. 2006a. "Assessing the Impact of a School Subsidy Program in Mexico: Using a
Social Experiment to Validate a Dynamic Behavioral Model of Child Schooling and Fertility."
American Economic Review 96(5):1384-1417.
28
Figure 1: Enrollment decisions and Adult Income in the Basic Model
U
[U (h ) - U ( )]
O B
U ( A + w ) - U ( A)
U ( A + 2 w) - U ( A + w)
A* A** A
`
Figure 2: Introducing a Conditional Cash Transfer
U
[U (h ) - U ( )]
U (A + w + ) -U (A + )
U ( A + 2 w) - U ( A + w + )
A* A* A** A** A
29
Figure 3: Program effects on applicants and their siblings
A. Enrollment B. Work for pay C. Work for no pay
Applicants
1
1
1
.8
.8
.8
.6
.6
.6
Probability
Probability
Probability
.4
.4
.4
.2
.2
.2
0
0
0
-25 -15 -5 5 15 25 -25 -15 -5 5 15 25 -25 -15 -5 5 15 25
Relative ranking Relative ranking Relative ranking
Mean Mean Mean
Quartic Quartic Quartic
Siblings
1
1
1
.8
.8
.8
.6
.6
.6
Probability
Probability
Probability
.4
.4
.4
.2
.2
.2
0
0
0
-25 -15 -5 5 15 25 -25 -15 -5 5 15 25 -25 -15 -5 5 15 25
Relative ranking Relative ranking Relative ranking
Mean Mean Mean
Quartic Quartic Quartic
30
Table 1: Characteristics of CSP recipients and non-recipient applicants
Overall Within 10 ranks of cutoff
Non Recip- Diff. P-value Dummy Dummy Non Recip- Diff. P-value Dummy Dummy
recip- ients RD RD recip- ients RD RD
ients Coef. P-value ients Coef. P-value
Male 0.392 0.234 -0.157 0.000** -0.057 0.025* 0.389 0.305 -0.084 0.003** -0.062 0.156
Live with mother 0.861 0.774 -0.086 0.000** 0.023 0.248 0.851 0.844 -0.007 0.752 0.013 0.648
Mother attended school 0.501 0.363 -0.138 0.000** 0.050 0.073 0.481 0.477 -0.004 0.898 0.057 0.201
Live with father 0.683 0.526 -0.157 0.000** 0.002 0.944 0.627 0.624 -0.003 0.935 0.039 0.398
Father attended school 0.578 0.413 -0.165 0.000** 0.015 0.554 0.569 0.494 -0.075 0.014* 0.049 0.258
Parent is civil servant 0.051 0.023 -0.029 0.000** -0.007 0.487 0.046 0.026 -0.020 0.181 -0.015 0.411
Number of other children in hh 1.302 1.334 0.033 0.445 0.097 0.146 1.378 1.398 0.020 0.790 0.040 0.749
Number of adults in household 2.963 2.726 -0.236 0.000** 0.116 0.125 2.878 2.902 0.024 0.811 0.107 0.373
Disabled household member 0.164 0.197 0.033 0.030* -0.025 0.291 0.193 0.157 -0.036 0.140 -0.052 0.112
Own bicycle 0.754 0.545 -0.209 0.000** 0.002 0.922 0.720 0.672 -0.049 0.071 0.003 0.938
Own ox/horses cart 0.371 0.255 -0.116 0.000** -0.018 0.474 0.354 0.307 -0.047 0.107 0.063 0.073
Own motorbike 0.114 0.034 -0.079 0.000** 0.005 0.677 0.080 0.063 -0.018 0.240 0.007 0.757
Own car or truck 0.018 0.001 -0.016 0.001** 0.003 0.500 0.016 0.003 -0.013 0.059 0.000 0.964
Own radio 0.392 0.255 -0.137 0.000** -0.048 0.081 0.373 0.305 -0.068 0.018* -0.024 0.621
Own TV 0.386 0.144 -0.242 0.000** -0.007 0.789 0.346 0.247 -0.099 0.001 -0.068 0.110
Roof made of solid materials 0.656 0.445 -0.211 0.000** -0.034 0.205 0.629 0.575 -0.054 0.089 -0.048 0.282
Floors: Polished wood/Tiles 0.014 0.010 -0.003 0.370 0.007 0.200 0.005 0.016 0.011 0.040* 0.015 0.118
Floors: wood planks or bamboo 0.943 0.900 -0.043 0.000** -0.046 0.001** 0.952 0.924 -0.028 0.060 -0.013 0.603
Drinking water: piped into house 0.003 0.001 -0.002 0.136 -0.002 0.220 0.000 0.000 0.000 0.000
Drinking water: well/pump 0.793 0.766 -0.028 0.085 -0.033 0.074 0.780 0.753 -0.027 0.309 -0.019 0.554
Drinking water: vendor purchased 0.015 0.014 -0.001 0.800 0.007 0.250 0.014 0.023 0.010 0.189 0.012 0.221
Toilet: Flush 0.031 0.005 -0.027 0.010** 0.008 0.098 0.027 0.009 -0.019 0.202 0.006 0.618
Toilet: Pit latrine 0.077 0.051 -0.026 0.004** 0.014 0.203 0.055 0.071 0.016 0.248 0.033 0.108
Lighting: Electricity from a generator 0.012 0.002 -0.010 0.197 0.002 0.547 0.005 0.001 -0.003 0.515 -0.002 0.712
Lighting: Electricity from a battery 0.518 0.317 -0.201 0.000** -0.005 0.850 0.483 0.419 -0.064 0.041 -0.032 0.461
Cooking fuel electricity,gas,kerosene 0.003 0.000 -0.003 0.102 0.000 0.810 0.000 0.001 0.001 0.314 0.004 0.318
Note: Information based on application forms for sample of applicants covered by household survey. ** significant at the 1 percent level, * at the 5 percent
level.
31
Table 2: Summary statistics on enrollment and work of non recipient applicants and their siblings
Males 7-18 Female 7-18 Parents
Non recipient Siblings of non Non recipient Fathers of non- Fathers of non- Mothers of
applicants recipient applicants recipient recipient non-recipient
applicants applicants applicants applicants
Enrolled 0.628 0.860 0.544 0.804 - -
(0.484) (0.347) (0.498) (0.397) - -
Enrolled, hours 25.96 21.34 26.12 21.50 - -
(9.36) (7.19) (9.27) (6.70) - -
Work for pay 0.309 0.093 0.366 0.167 0.285 0.218
(0.463) (0.290) (0.482) (0.373) (0.452) (0.413)
Work for pay, hours 24.03 21.96 27.76 24.61 30.19 24.03
(23.04) (23.86) (26.52) (24.90) (23.07) (23.04)
Work for no pay 0.637 0.517 0.513 0.466 0.778 0.742
(0.481) (0.500) (0.500) (0.499) (0.416) (0.437)
Work for no pay, hours 19.13 18.18 19.56 16.83 35.62 32.03
(14.53) (13.19) (14.76) (12.77) (18.90) (18.47)
Note: Standard deviations in parentheses
32
Table 3: Program effects on recipients and siblings, by gender
School enrollment Work for pay Work without pay
Own effect*male 0.215** -0.120** 0.043
(0.031) (0.032) (0.037)
Own effect*female 0.200** -0.088** 0.074*
(0.026) (0.025) (0.029)
Sibling effect*male 0.011 -0.007 0.046
(0.019) (0.020) (0.030)
Sibling effect*female -0.000 -0.034 0.028
(0.019) (0.021) (0.028)
R-squared 0.31 0.21 0.11
P-value: Own(M)=Own(F) 0.70 0.42 0.48
P-value: Sib(M)=Sib(F) 0.60 0.28 0.63
P-value: Own(M)=Sib(M) 0.00 0.00 0.95
P-value: Own(F)=Sib(F) 0.00 0.02 0.10
Note: Sample size is 8182 in all regressions. Sample includes all children ages 7 to 18. All specifications include a set of school dummies, a
set of single year age dummies, a set of birth order dummies, a dummy for the gender of the child, dummy variables for sibling*gender, and a
quartic in the score. Standard errors adjust for clustering at the applicant primary-school level. ** significant at the 1 percent level, * at the 5
percent level. P-values are from an F-test of equality of parameter estimates.
33
Table 4: Program effects on recipients and siblings, by gender
Tobit (Marginal Effects) OLS
Hours of Hours worked for Hours worked Hours of Hours worked for Hours worked
schooling pay without pay schooling pay without pay
Own effect*male 7.667** -1.213* -0.480 6.130** -3.225** -1.552
(1.193) (0.370) (0.845) (0.945) (1.091) (1.052)
Own effect*female 8.275** -1.162* -0.339 6.626** -3.297** -1.690*
(0.993) (0.325) (0.693) (0.783) (1.035) (0.787)
Sibling effect*male 1.104 0.010 0.674 1.022* -0.848 0.276
(0.686) (0.603) (0.790) (0.595) (0.671) (0.825)
Sibling effect*female 0.158 -0.546 0.174 0.209 -0.825 -0.125
(0.683) (0.424) (0.702) (0.596) (0.712) (0.731)
R-squared 0.21 0.12 0.10
P-value: Own(M)=Own(F) 0.61 0.79 0.89 0.66 0.96 0.91
P-value: Sib(M)=Sib(F) 0.24 0.39 0.61 0.24 0.98 0.71
P-value: Own(M)=Sib(M) 0.00 0.01 0.16 0.00 0.02 0.06
P-value: Own(F)=Sib(F) 0.00 0.08 0.45 0.00 0.01 0.04
Note: Sample size is 8182 in all regressions. Sample includes all children ages 7 to 18. All specifications include a set of school dummies, a set of
single year age dummies, a set of birth order dummies, a dummy for the gender of the child, dummy variables for sibling*gender, and a quartic in the
score. Standard errors adjust for clustering at the applicant primary-school level. ** significant at the 1 percent level, * at the 5 percent level. P-values
are from an F-test of equality of parameter estimates.
34
Table 5: Program effects on recipients and siblings, by gender alternative estimation approaches
Restricted to within 10 ranks of cutoff Control function is school-specific function
Enrolled Worked for pay Worked without Enrolled Worked for pay Worked without
pay pay
Own effect*male 0.215** -0.175** 0.098 0.188** -0.120** 0.036
(0.056) (0.052) (0.055) (0.040) (0.040) (0.047)
Own effect*female 0.192** -0.046 0.074 0.209** -0.070* 0.123**
(0.039) (0.039) (0.047) (0.034) (0.035) (0.040)
Sibling effect*male 0.001 -0.014 0.078 -0.017 -0.006 0.045
(0.029) (0.029) (0.044) (0.028) (0.029) (0.041)
Sibling effect*female -0.018 -0.049 0.052 0.000 -0.010 0.070
(0.028) (0.031) (0.046) (0.028) (0.031) (0.040)
R-squared 0.31 0.23 0.14 0.35 0.27 0.19
P-value: Own(M)=Own(F) 0.71 0.02 0.71 0.68 0.33 0.15
P-value: Sib(M)=Sib(F) 0.54 0.30 0.60 0.64 0.93 0.66
P-value: Own(M)=Sib(M) 0.00 0.00 0.73 0.00 0.00 0.79
P-value: Own(F)=Sib(F) 0.00 0.92 0.65 0.00 0.01 0.07
Note: Sample size is 2920 for the sample of children in households within 10 ranks of cutoff, and 8182 for the full sample. All specifications include a set
of school dummies, a set of single year age dummies, a set of birth order dummies, a dummy for the gender of the child, dummy variables for
sibling*gender, and a quartic in the control function. Standard errors adjust for clustering at the applicant primary-school level. ** significant at the 1
percent level, * at the 5 percent level. P-values are from an F-test of equality of parameter estimates.
35
Table 6: Program effects on recipients and siblings, by genderdefining control function as within-school ranking
Control function is function of within-school ranking Control function is school-specific function of within school
ranking
Enrolled Worked for pay Worked without Enrolled Worked for pay Worked without
pay pay
Own effect*male 0.187** -0.142** 0.114* 0.181** -0.120* 0.075
(0.040) (0.045) (0.053) (0.045) (0.047) (0.054)
Own effect*female 0.175** -0.047 0.112* 0.188** -0.058 0.135**
(0.037) (0.036) (0.047) (0.039) (0.039) (0.048)
Sibling effect*male -0.018 -0.030 0.120* -0.021 -0.007 0.093
(0.032) (0.036) (0.049) (0.035) (0.037) (0.050)
Sibling effect*female -0.027 0.008 0.064 -0.020 0.003 0.083
(0.032) (0.032) (0.046) (0.033) (0.035) (0.048)
R-squared 0.31 0.21 0.12 0.35 0.27 0.19
P-value: Own(M)=Own(F) 0.83 0.08 0.98 0.90 0.29 0.40
P-value: Sib(M)=Sib(F) 0.84 0.37 0.38 0.98 0.83 0.89
P-value: Own(M)=Sib(M) 0.00 0.00 0.85 0.00 0.00 0.63
P-value: Own(F)=Sib(F) 0.00 0.02 0.09 0.00 0.01 0.08
Note: Sample size is 8182 in all regressions. Sample includes all children ages 7 to 18. All specifications include a set of school dummies, a set of
single year age dummies, a set of birth order dummies, a dummy for the gender of the child, dummy variables for sibling*gender, and a quartic in the
control function. Standard errors adjust for clustering at the applicant primary-school level. ** significant at the 1 percent level, * at the 5 percent
level. P-values are from an F-test of equality of parameter estimates.
36
Table 7: Program effects on recipients and siblings, by age relative to applicant's age
School enrollment Work for pay Work without pay
Own effect 0.198** -0.092** 0.059*
(0.020) (0.020) (0.024)
Sibling effect*younger 0.016 -0.028 0.029
(0.016) (0.016) (0.025)
Sibling effect*older -0.025 0.018 0.069
(0.032) (0.038) (0.037)
R-squared 0.32 0.21 0.11
P-value: Sib(Y)=Sib(O) 0.21 0.21 0.30
Note: sample size is 8182 in all regressions. All specifications include a set of school dummies, a set of single year age dummies, a set of
birth order dummies, a dummy for the gender of the child, dummy variables for sibling*gender, and a quartic in the score. Standard errors
adjust for clustering at the applicant primary-school level. ** significant at the 1 percent level, * at the 5 percent level. P-values are from an
F-test of equality of parameter estimates.
37
Appendix 1: Proof of Proposition 1.
Consider first the conditions under which both children would be enrolled. 1 = 2 = 1 if and only if:
U ( A) + 2 U (h ) U ( A + w) + [U (h ) + U ( )] (A1)
and U ( A) + 2 U (h ) U ( A + 2 w) + 2U ( ) (A2)
(A1) implies U ( A + w) - U ( A) [U (h ) - U ( )] (A3)
(A2) implies U ( A + 2 w) - U ( A) 2 [U (h ) - U ( )] (A4)
Concavity of U(.) implies that 2[U ( A + w) - U ( A)] > U ( A + 2 w) - U ( A) , so (A4) is always implied by
(A3). (A3) is the necessary and sufficient condition for 1 = 2 = 1 . Given the Inada conditions on U(.),
A * * such that U ( A * * + w) - U ( A * *) = [U (h ) - U ( )] . Concavity again implies that
U ( A + w) - U ( A) > [U (h ) - U ( )], A < A * * ; and U ( A + w) - U ( A) < [U (h ) - U ( )] ,
A > A * * . (At equality (A3) corresponds to point B in Figure 1.)
Now consider the conditions (if any) under which a single child would be enrolled. i = 1, j = 0, i j ,
if and only if:
U ( A + w) + [U (h ) + U ( )] U ( A) + 2 U (h ) (A5)
and U ( A + w) + [U (h ) + U ( )] U ( A + 2 w) + 2 U ( ) (A6)
(A5) is just the converse of (A1), and implies the converse of (A3). (A6) implies:
U ( A + 2 w) - U ( A + w) [U (h ) - U ( )] (A7)
The Inada conditions imply that A * such that U ( A * +2 w) - U ( A * + w) = [U (h ) - U ( )]. Concavity
of U(.) implies that U ( A + 2 w) - U ( A + w) < [U (h ) - U ( )] , A > A * , and
U ( A + 2 w) - U ( A + w) > [U (h ) - U ( )] , A < A * . (At equality, (A7) corresponds to point O in
Figure 1.)
It follows that
(i) 1 = 2 = 0 , A < A *
(ii) i = 1, j = 0, i j , , A [ A*, A * *)
(iii) 1 = 2 = 1 , A A * *
1
Appendix 2: Program effects on parents
The model proposed in the paper assumes that parents continue to supply labor inelastically in
response to a transfer that is conditioned on child schooling. This is consistent with the literature on CCTs
(see Fiszbein and Schady 2009, especially Chapter 4, for a review of the evidence from a number of
countries.) In addition, we find no evidence of significant changes in parental labor supply in Cambodia.
Table 5 summarizes the results of estimating a simplified version of equation (1), focusing both on the
incidence of different kinds of work (left-hand panel) and hours (right-side panel), with the latter
estimated by Tobit and OLS, as before. We estimate this model for fathers and mothers, and for male and
female applicants, separately. The only significant finding in Table 5 is that mothers are less likely to
work without pay when their daughters receive a scholarship (a difference of 7 percentage points)
although the change in hours (about 2 hours, on average) is quite small. There is little evidence of large
reallocations of parent labor in these data.
Appendix Table: Program effects on parents
Did activity Hours of activity
Tobit (marginal effect) OLS
Worked for Worked Hours Hours Hours Hours
pay without pay worked for worked worked for worked
pay without pay pay without pay
Male applicant
Father -0.047 -0.040 2.083 -1.700 5.628 -1.711
(0.078) (0.078) (2.158) (3.769) (3.428) (3.868)
R-squared 0.20 0.20 0.18 0.22
Mother 0.030 0.021 0.687 -0.189 1.409 -0.334
(0.048) (0.056) (0.956) (2.544) (2.023) (2.600)
R-squared 0.20 0.17 0.19 0.17
Female applicant
Father 0.032 -0.023 -0.032 -2.596 -1.664 -2.763
(0.038) (0.036) (1.201) (1.949) (1.466) (1.906)
R-squared 0.13 0.08 0.10 0.11
Mother -0.011 0.073 -0.017 2.411 -0.486 1.803
(0.031) (0.032)* (0.816) (1.428) (1.076) (1.461)
R-squared 0.17 0.07 0.12 0.11
Note: Sample sizes are 489 for the sample of male applicants/fathers; 758 for the sample of male
applicants/mothers;1425 for the sample of female applicants/fathers; and 1889 for the sample of female
applicants/mothers. All specifications include a set of school dummies, a set of single year age dummies, and a
quartic in the score. Standard errors adjust for clustering at the applicant primary-school level. ** significant at
the 1 percent level, * at the 5 percent level.
2