Cash Transfers and School Outcomes:
the case of Uruguay
Mery Ferrando
⇤†
Abstract
This study evaluates the e↵ects of a conditional cash transfer program in Uruguay
on a wide set of school outcomes for students in grades one to four of secondary
school.
The program was launched in 2005 and was thought as a three-year
temporary program.
The evaluation is based on two main datasets, namely,
the administrative records of the program and secondary school registers. Since
assignment to the program was based on a proxy means test, the empirical strategy
follows a Regression Discontinuity approach. Results indicate that the program
increased school attendance for children belonging to beneficiary households. This
e↵ect is only significant for girls and first graders. Among girls, the program led to
a reduction in absenteeism ranging from 0.6 to 0.9 days a month. The program did
not have significant e↵ects in other school outcomes such as promotion or repetition.
Keywords:
Cash transfer, school attendance and performance, regression
discontinuity.
JEL Classification Numbers: I21, I38, O15.
⇤
Université catholique de Louvain, [email protected].
The author thanks William Parienté, François Maniquet, Marion Leturcq and Andrea Vigorito for
valuable comments and suggestions and Gonzalo Salas for his insights on the secondary school data.
Financial support from Universidad de la República (Uruguay) is gratefully acknowledged. The usual
disclaimer applies.
†
1
Introduction
This study analyzes the e↵ects of a conditional cash transfer (CCT) –Plan de Atención
Nacional a la Emergencia Social (PANES)- in Uruguay on a large set of school outcomes.
Using a rich dataset that combines information at individual level from secondary school
registers and the program administrative records, the study provides evidence on
the causal e↵ect of an anti-poverty program on school performance and frequency of
attendance.
CCT programs have become widely popular in developing countries, particularly in
Latin America, and have been adopted by more than 30 countries since they were first
introduced in the 1990s. Their innovative feature lies in combining both short and
long-run poverty alleviation goals. Precisely, CCTs are aimed at alleviating short-run
poverty by the provision of monetary transfers and fostering long run well-being through
accumulation of human capital among poor households, especially in terms of education
and health, by conditioning these transfers to child school attendance and health checks.
CCTs have therefore a first goal of immediate poverty reduction. Due to the transfers,
well-targeted programs should in principle result in increased financial resources among
poor households. However, behavorial responses such as negative e↵ects on labor supply
and expected reduction in child labor among recipients may o↵set the potential income
increase. In practice, evidence suggests that CCTs have been in general well-targeted
to poor households. The transfers had raised household consumption and resulted in
lower income poverty, although the magnitude of the impacts varies in di↵erent contexts,
depending on the amount of the benefits and the o↵setting behavioral responses to the
program (Fiszbein and Schady, 2009; Rawlings and Rubio, 2005).
A major distinctive feature of CCTs is their focus on long-term human capital accumulation among poor children as a way to break intergenerational transmission of poverty.
Thus, they di↵er from traditional social assistance programs which were mainly focused
on alleviating household financial restrictions in the short run (Aber and Rawlings, 2011).
CCTs have been shown to be e↵ective in promoting human capital accumulation among
poor households (Rawlings and Rubio, 2005; Fiszbein and Schady, 2009; World Bank,
2011b). In terms of education, evaluations reviewed below provide evidence mainly on
enrollment and to a lesser extent attendance while assessments of impacts on other
school outcomes such as promotion, repetition or learning achievements are scarce.
Evidence systematically shows an increase on school enrollment and attendance rates
but no significant impacts on learning achievements among school age children were
1
found. Regarding health outcomes evidence is more mixed. Results show an increase
in the use of preventive health services, mainly of growth monitoring for children, and
that in some cases CCTs have positively a↵ected health outcomes as the incidence of
low child height (Fiszbein and Schady, 2009; Lagarde et al., 2009).
This study focuses on the e↵ects of a cash transfer program on human capital accumulation in education, which is arguably one of the key mechanisms through which CCTs
may foster children long run well-being. The program represents the first attempt to
implement a large scale conditional cash transfer targeted to poor households in Uruguay.
PANES comprises a wide set of short and long run goals, including the improvement of
human capital accumulation among deprived children.
While Uruguay has reached universal coverage of primary school at an early stage,
secondary school level is a↵ected by high drop-out rates, education lag and insufficient
learning achievements. Information from school registers and program administrative
data allows to analyze whether a large scale program had impacted school outcomes
among students attending the first four years of secondary school. In particular, the
school registers used allow to assess the e↵ects on promotion, repetition due to poor
performance or attendance, number of absences and average point score for those
promoted.
Assignment to the program was based on a predicted poverty score using household
characteristics. Only those households whose score was above a certain threshold were
eligible for the benefits. Exploiting the eligibility rule, the e↵ect of the program is then
evaluated using a Regression Discontinuity Design (RDD), which relies on comparison
of students belonging to households just above and below the score threshold for
determining eligibility. Reliable program e↵ects can then be obtained by estimating the
discontinuity on school outcomes around the cut-o↵.
Results indicate that PANES reduced the number of unjustified absences throughout
the school year, although the e↵ect is limited and concentrated on girls and first
graders. The program did not substantially a↵ect other school outcomes such as
promotion or repetition due to poor performance. Using information from one of the
follow-up surveys designed to evaluate the program and social security registers, this
study also analyzes the potential underlying mechanisms through which PANES may
have a↵ected school outcomes. While the data available tends to indicate that no
role was played by conditions attached to the program, it appears that there was an
education wealth e↵ect since households had a net increase on income due to the program.
2
While PANES has been extensively evaluated on a wide set of outcomes, including child
labor and reported school attendance for children aged 6 to 17, labor supply, political
support and birth weight (see for instance Manacorda et al. (2009); Amarante et al.
(2011a,b)), there is no previous study on PANES that analyzes a large set of school
outcomes as I study here. Also, this study provides novelty in assessing the impact
of a conditional cash transfer using information from secondary school records which
allows to estimate the impacts on a large set of outcomes such as repetition, promotion
and absences. On the contrary, most studies on CCT have focused on enrollment or
attendance. Finally, even when PANES was considered a conditional cash transfer,
conditions were de facto not monitored. Therefore, unlike most CCTs, this study
provides evidence mainly on the e↵ects of a cash transfer program on school outcomes.
As a consequence, school outcomes will be mainly a↵ected through an income e↵ect
rather than through the conditions attached.
The rest of the paper is organized as follows. Section 2 discusses the main mechanisms
through which conditional cash transfer might a↵ect school outcomes and reviews the
literature on CCTs and educational outcomes. The main characteristics of PANES and
its implementation is described in Section 3. Section 4 presents the estimation method
and the data. Results are presented in section 5. Section 6 concludes.
2
CCTs and school attendance and performance
In theory, there are two main mechanisms through which CCTs may a↵ect incentives of
beneficiary households to modify children’s time allocation in favor of schooling. First,
the cash transfer may boost poor households’ income. This can lead to an education
wealth e↵ect, i.e. an increase on the demand for schooling due to an increase on
household’s income. This e↵ect may take place because households face borrowing
constraints which prevent them from investing in education and/or because households
value education as a consumption good (Glewwe and Jacoby, 2004)1 . Furthermore, in
the specific case of CCTs that give transfers to women, the e↵ect on schooling may be
explained by the fact that when transfers are made to women a larger share is spent
on children than when men are the transfer recipients (Fiszbein and Schady, 2009).
Empirical studies confirm the existence of a positive association between household
income and child schooling. Although early studies indicate that the magnitude of this
association is small, recent studies tend to find a strong link between household wealth
and schooling (Behrman and Knowles, 1999; Glewwe and Jacoby, 2004; Cogneau and
Jedwab, 2007; Huebler, 2008; Grimm, 2011).
1
Note that non-constrained households who value education strictly as an investment good will not a↵ect
their schooling decision in response to the transfer.
3
Therefore, the success of CCTs in increasing school attendance depends on the net
e↵ect of the transfer on household income. However, the increase in income can be
o↵set by behavioral responses of the households. The pure income e↵ect associated
with the benefits may encourage adults to reduce labor supply provided leisure is a
normal good. There are other sources that may reinforce this disincentive e↵ect. When
programs are means tested, as is the case of the program studied here, households may
believe that they must strategically reduce the amount of work supplied to become
or remain eligible. Finally, compliance with the requirements on schooling and health
check-ups may reduce the amount of time parents can devote to work (or eventually to
leisure) (Fiszbein and Schady, 2009). Nevertheless, there might also be some incentive
to increase labor e↵ort among adults. If the increase on schooling implies that children
reduce some work activities, parents may o↵set this reduction working more (Parker
and Skoufias, 2000)2 . Also, for adult members, especially women, taking care of their
children may be less time-consuming if the program leads children to spend more time
in school. Adults may then have some extra time to supply labor (Attanasio et al., 2003).
Conditions introduce a second mechanism that may foster children’s school attendance
in households that would not have sent their children to school in absence of the
program, i.e. households for which the condition is binding. Conditions on schooling
are based on the idea that private investment in human capital in poor households
may be suboptimal. Parents may su↵er from incomplete altruism, self-control problems
and procrastination or face imperfect information about education returns that may
prevent them from investing in children’s education (Fiszbein and Schady, 2009). In this
context, the conditioning on school attendance reduces the shadow price of education.
This price e↵ect comprises an income and a substitution e↵ect, both of which incentive
parents to increase child schooling (Parker and Skoufias, 2000). A review based on recent
randomized evaluations of di↵erent social programs including conditional cash transfers
suggest that prices have large impacts on access to education in developing countries
(Holla and Kremer, 2009). The conditions attached to the programs may also increase
the value parents place on education, changing their behavior towards investment in
education (Baez and Camacho, 2011).
The e↵ect of the income and substitution e↵ects associated with the cash transfer and
conditions on schooling will vary depending on households’ initial conditions. Skoufias
and Parker (2001) present a formal model that illustrates how the decision on children’s
2
Note that the increase in school attendance does not necessarily imply a reduction in child labor, since
both activities might not be substitutes and the increase in schooling may be at the expense of children’s
leisure time (Skoufias and Parker, 2001). The e↵ects of CCTs on child labor are beyond the scope of
this study and are not presented in detail.
4
schooling depends on households’ preferences and their location along the budget set
before the program. Results suggest there is a minimum value of the transfer above
which parents are compelled to send their children to school. Provided benefits are above
this threshold, the e↵ects depend on whether the conditions on education are binding or
not. On one hand, for households that were not sending children to school in absence
of the program,i.e households for which the conditions are binding, the conditional
transfer might foster child schooling both through income and substitution e↵ects. On
the other hand, for households with children who were already attending school before
the program, the transfer might only have a pure income e↵ect, which may lead to an
increase in the time children allocate to studying or attending classes rather than an
increase in enrollment.
The main e↵ect of the transfers is therefore an increase in the demand for schooling.
With imperfect capital markets, these e↵ects should be higher among poor households
who are limited in their access to credit (World Bank, 2011a). Moreover, the net income
increase may prevent parents from taking children out of school when facing negative
shocks in other income sources. Otherwise, credit-constrained households may reduce
schooling in favor of child labor in order to smooth consumption (de Janvry et al., 2006).
Existing evidence also shows that when financial markets are imperfect poor children
frequently reduce school attendance, drop-out from school or are not enrolled in response
to negative income shocks (Jacoby and Skoufias, 1997; Jensen, 2000; Duryea et al., 2007).
The increase in school demand due to the conditional transfer is expected to increase
educational attainment. Higher attendance rates and time devoted to study should lead
to more learning and grade promotion and eventually, if the program e↵ect lasts over
time, to higher cognitive development and (final) human capital accumulation in the
long run. Furthermore, the potential net increase in household income associated with
the transfer may modify consumption patterns, increasing the consumption of goods
and services such as food and books that favor learning (Baez and Camacho, 2011).
The program may also enhance parents’ attitude and involvement in their children’s
learning process, which in turn may promote educational achievement. Nevertheless,
some factors may prevent poor children from taking advantage of higher schooling. If
supply of schooling is held constant, the increase in the use of education services may
lead to overcrowding of schools in poorer neighborhoods, which in turn may prevent
students from grade advancement (World Bank, 2011a). Also, provided there is some
selection process in the decision to attend school, poor children brought into school
by the program may have lower expected returns from education and learn less than
children already attending school (Filmer and Schady, 2009).
5
There is plenty of evidence on the impacts of CCTs on school enrollment and to a lesser
extent school attendance, especially for Latin American countries. In general, CCTs
have been shown to be e↵ective in increasing school enrollment and attendance, at least
in the short and medium run (Villatoro, 2005; ECLAC, 2006; Fiszbein and Schady,
2009). Most evaluations focus on the impacts of the programs in school enrollment (or
school attendance measured by the proportion of children that report being attending
school). The evidence is more limited in relation to school attendance measured by
how many days children enrolled in school have e↵ectively attended classes (henceforth
referred to as e↵ective school attendance).
Regarding the first group of evaluations, in Latin America and the Caribbean,
Nicaragua’s Red de Protección Social, Ecuador’s Bono de Desarrollo Humano and Chile
Solidario had led to significant increases in school enrollment, which ranges from 7 to 13
percentage points (pp.) (Schady and Araujo, 2008; Maluccio and Flores, 2005; Galasso,
2006). For Colombia (Attanasio et al., 2005) and Honduras (Glewwe and Olinto, 2004)
smaller but significant e↵ects on school enrollment were also found.
The case of Oportunidades (ex PROGRESA) in Mexico has been extensively studied
through experimental designs and there is solid evidence of a significant increase in
school participation at secondary school age (Parker and Skoufias, 2000; Skoufias and
Parker, 2001; Schultz, 2004; Coady and Parker, 2004; Behrman et al., 2005). Schultz
(2004) finds that at the primary school level, the program led to a small increase in
enrollment rate of 0.92 pp. for girls and 0.80 pp. for boys, while at secondary level
the increase amounts to 9.2 pp. and 6.2 pp. for girls and boys respectively. Parker
and Skoufias (2000) show however that the program did not a↵ect total hours devoted
to school, implying that the main impact was to increase the number of children who
attend school. The evidence is more limited for Bolsa Famı́lia in Brazil, the largest CCT,
but a recent study also finds a positive impact on school enrollment, which increased
5.5% among beneficiaries in grades 1–4 and 6.5% in grades 5–8 (Glewwe and Kassouf,
2012). This goes in line with previous evidence on the positive impact of Bolsa Escola
on school attendance (Cardoso and Souza, 2004).
For other developing countries, CCTs have been mainly designed as gender-targeted
programs. In general, evaluations have found substantial e↵ects of these programs in
school enrollment. This is the case of Bangladesh’s Female Secondary Stipend Program
(Khandker et al., 2003) and Pakistan’s Punjab Education Sector Reforms Programme
(Chaudhury and Parajuli, 2010). The estimated program e↵ects are particularly high in
Cambodia, for which Filmer and Schady (2008, 2011) find that the increase on school
enrollment due to two programs amount to more than 20 pp. and even reach 30 pp. in
6
some cases.
The evidence in terms of how the programs a↵ect the time children spend at school is
reduced to a few studies which rely on reported attendance (or absence) rates. Overall,
the results show that CCTs have succeeded in increasing e↵ective school attendance,
although the gains appear to be modest.
An evaluation for Honduras’ Programa de Asignación Familiar assesses the impact on
attendance considering the reported number of days the child was absent during the last
30 days. Results indicate that the program increased school attendance (conditional on
enrollment) by 0.8 days per month for children aged 6 to 13 in rural areas (Glewwe and
Olinto, 2004). Jamaica’s PATH has been found to increase (reported) daily attendance
by 0.5 days per month (Levy and Ohls, 2007). Maluccio and Flores (2005) analyze
the impact of Red de Protección Social in Nicaragua on current attendance (defined as
not having missed more than 3 unjustified classes the last month). They find that the
program had a larger e↵ect on current attendance than enrollment with an increase of 20
pp. for children 7–13 years old. Schultz (2000) follow a similar analysis for PROGRESA
in Mexico, where respondents were asked how many days children enrolled in school have
been absent from school in the last month. However, no impact on school attendance
was found.
Existing evidence has also analyzed the e↵ects of CCTs on grade progression and
retention, which might provide insights on whether the observed increase in enrollment
will result in higher school attainment. Results show in general that CCTs has lead to
higher grade promotion and lower repetition and drop-out rates, particularly in primary
school (see for instance Glewwe and Olinto, 2004 on Honduras, Behrman et al., 2005 on
Mexico, Maluccio and Flores, 2005 on Nicaragua, Glewwe and Kassouf, 2012 on Brazil).
Evidence is limited regarding the long-run e↵ects of CCTs on educational attainment.
Few studies indicate that the programs had a moderate impact on years of schooling
attained by adults (Fiszbein and Schady, 2009). The only program for which the
e↵ects on completed school attainment has been studied is Oportunidades (Fiszbein
and Schady, 2009). Behrman et al. (2009) find that after 5.5 years of exposure to
Oportunidades children who received the benefits for 18 additional months achieve on
average 0.2 more grades of schooling. The positive impact on years of schooling attained
is confirmed for longer periods of exposure (about a decade) to the Mexican CCT,
although there are no significant impacts on the proportion of beneficiaries who enter
college (Parker and Behrman, 2008). Recently, Baez and Camacho (2011) evaluate the
long-run e↵ect of Familias en Acción in Colombia on human capital accumulation using a
7
close indicator of high school completion for students just prior to graduation. They find
that participants are 4 to 8 pp. more likely to finish high school. Few other evaluations
rely on samples of beneficiaries still at schooling age or on assumptions about long-run
behaviors to estimate the impact on final schooling attainment. Studies from Honduras,
Cambodia and Pakistan for example indicate that recipients are more likely to attain
additional years of schooling or complete school levels (Glewwe and Olinto, 2004; Filmer
and Schady, 2009; World Bank, 2011a).
Little is known about the impact of CCTs in the development of children’s cognitive
abilities (ECLAC, 2006; Fiszbein and Schady, 2009). Despite the observed increase in
the use of education services, results indicate overall that the programs did not lead to
significant learning improvements. Two evaluations assess the short run e↵ects of CCTs
on students’ cognitive achievements as measured by school-based tests on mathematics
and language. Note that studies based on tests administered at school may su↵er from
selection bias since the programs tend to increase enrollment among poorer children,
introducing problems of comparability between beneficiary and non-beneficiary students3 . Either in Mexico (Behrman et al., 2000) or Ecuador (Ponce and Bedi, 2010) the
programs did not have a significant e↵ect on achievement test scores. Filmer and Schady
(2009) provide evidence for Cambodia’s CESSP based on home-based achievement tests
in mathematics and language and an additional school-based test on maths. Despite
large positive impacts of the program on school enrollment and attendance as well as
positive impact on years of schooling, no significant di↵erences were found between the
treatment and control groups on achievement test scores.
Similar results are found for the long-term e↵ects of CCTs on cognitive achievement. For
the Colombian program Familias en Acción, Baez and Camacho (2011) find that although
beneficiary students are more likely to complete high school than non-beneficiaries they
do not perform better on (in-classroom) achievement tests. Similarly, Behrman et al.
(2009) find a positive impact of 18 additional months of Oportunidades exposure on
grades of schooling attained but no significant impact on home-based achievement tests.
The theoretical discussion suggests that conditionalities might be a key element of the
programs to foster school attendance. There is however limited evidence on the role
played by conditionalities to explain the increase in school attendance observed across
countries. Overall, evidence suggests that conditions lead to a greater impact on school
participation than would have been observed under unconditioned transfers. Schady
and Araujo (2008) exploit the fact that the conditionality of school attendance was not
enforced and only a quarter of respondents stated they were aware of the requirement
3
See Fiszbein and Schady (2009) for a discussion on the methodological concerns of this type of studies.
8
in Ecuadorian’s Bono de Desarrollo Humano (BDH). The results show that BDH had
a large positive impact on school enrollment (approximately 10 pp.) which was only
significant among conditioned households. For Mexico, De Brauw and Hoddinott (2011)
analyze the role of conditionalities comparing the e↵ects on school enrollment between
households that received and did not receive the forms needed to monitor the conditions.
Results also show that the impact was higher among conditioned households, especially
among children in the transition to lower secondary school. Ferreira et al. (2009) take
another approach to analyze the role of conditionalities in the CESSP program in
Cambodia. They consider the e↵ect of a child-specific scholarship on school enrollment
of recipient children and their non-conditioned siblings. Results show substantial impact
of the CCT on school enrollment of conditioned children but no e↵ect on ineligible siblings.
Finally, the relevance of disincentive e↵ects associated to the programs might give some
insight on the extent to which the pure income e↵ect operates. The evidence on labor
market outcomes shows that in general the programs did not have significant disincentive
e↵ects on labor supply of beneficiary households (Fiszbein and Schady, 2009). Several
evaluations for PROGRESA/Oportunidades in Mexico (Parker and Skoufias, 2000; Skoufias and Di Maro, 2008), Bolsa Famı́lia in Brazil (Foguel and Barros, 2010 and Medeiros
et al., 2008) and Cambodia Education Sector Support Project (CESSP) (Ferreira et al.,
2009) found no e↵ects on adult labor supply. Moreover, some evaluations of Chile Solidario and Bolsa Famı́lia have found even a positive e↵ect on adult labor supply (Galasso,
2006; Soares et al., 2010). An exception is the case of Red de Protección Social (RPS) in
Nicaragua, where a small but significant negative e↵ect of the program on total household
hours of work was found (Maluccio and Flores, 2005; Maluccio, 2007).
3
Country background and the program
Uruguay is a small middle income country with a population of 3.4 million and an annual
PPP per capita equivalent to U$S 150004 . Uruguay is classified as a high human development country; it ranks 48 in the world and third, behind Chile and Argentina among
Latin American countries according with the Human Development Index (HDI). Besides,
the country has traditionally distinguished in Latin America by its relatively low levels
of inequality and poverty (ECLAC, 2008). However, there has been an upward trend in
poverty and inequality since the second half of the 90s. The tendency of reduction of
living standards was worsened as a consequence of the 2002 economic crisis. One third
of the population fell below the national poverty line in 2003-2004. This trend deepened
the infantilization of poverty, which reached 50% of children below 18 in 2004 (Figure 1).
4
At 2011 World Bank statistics.
9
Figure 1: Evolution of poverty and inequality. 1990-2010.
A. Poverty
B. Inequality
60
48
50
46
40
44
30
42
20
40
10
38
0
36
1990 1992 1994 1996 1998 2000 2002 2004 2006 2008 2010
Child poverty
Poverty
Extreme poverty
1990 1992 1994 1996 1998 2000 2002 2004 2006 2008 2010
Gini index
Source: Based on Uruguayan household surveys.
Education in Uruguay was compulsory in 2005 for children aged 6 until completion
of six years of primary school and three years of lower secondary school5 . In terms
of educational achievements, Uruguay has been characterized by universal coverage at
primary school level. It has also attained nearly universal primary school completion
rate since 1990s. State schools play a major role covering more than 80% of total
students. Despite this democratization in access, primary level has been traditionally
characterized by high repetition rates, especially in the first grades and among students
from deprived households, and insufficient attendance. Even though repetition rates
have been significantly reduced recently, in 2011 14% of first-years students repeated
and 9% had poor attendance (ANEP, 2012).
Among the main concerns of the Uruguayan educational are high drop-out rates at
secondary school, especially at lower secondary school, and high inequality of learning
achievements by socioeconomic status. Coverage of secondary school is high although
below universal coverage. Moreover, there are significant attendance gaps by household
income which have not experienced substantial changes over time (Figure 2). Due to high
repetition and drop-out rates, only 55% of 16 years old students and less than 70% of
children aged 19 to 21 has already completed lower secondary school (Llambı́ et al., 2009).
In terms of learning achievements, Uruguay has participated since 2003 in the Programme
for International Student Assessment (PISA) that assesses learning achievements of
15-year-old students who are attending school. While Uruguay performs relatively well
in comparison with the rest of Latin American countries that take part in the evaluation,
results are substantially below OCDE countries. Besides, there are a high proportion
of students who do not reach the minimum level of competency defined by PISA. In
2009, more than 40% of students scored below the minimum level of competency in the
5
Since 2009 compulsory was extended to children aged 4 to 5 and until completion of 6 years of secondary
school
10
three assessed areas (reading, mathematics and science). Moreover, results show high
dispersion of performance by socioeconomic status. For instance, while nearly 70% of
students from the lowest socioeconomic status did not reach the minimum competency
level in reading, the proportion is less than 10% among students from the highest
socioeconomic status (ANEP, 2010).
Figure 2: Evolution of school attendance rates. 1990-2010
B. By household income. 13 to 16 years old.
A. By age group.
100
100
90
90
80
80
70
60
70
50
40
60
1990 1992 1994 1996 1998 2000 2002 2004 2006 2008 2010
4 to 5
6 to 12
13 to 16
17 to 18
1990 1992 1994 1996 1998 2000 2002 2004 2006 2008 2010
Quintile 1
Quintile 2
Quintile 4
Quintile 5
Quintile 3
Source: Based on Uruguayan household surveys.
3.1
Description of the program
Plan de Atención Nacional a la Emergencia Social (PANES) was a temporary antipoverty program carried out from April 2005 to December 2007. It was launched by the
center-left government that took power for first time in 2005 in order to face the increase
tendency in poverty observed since the late 90s and which had a substantial increase
after the 2002 economic crisis.
PANES was an ambitious program which had several non-contributive components. It
aimed on one hand at alleviating short run poverty mainly through monetary and food
transfers, and on the other hand to reduce poverty in the medium term by fostering
social and human capital accumulation among the poor through training, education and
social and labor participation components.
The target population comprised the first quintile of individuals below the national
poverty line, which amounted to approximately 8% of the total population. In practice,
the program covered 102,353 households which represent nearly 10% of total Uruguayan
households and 14% of the population. The total cost of the program represented 0.41%
of GDP and amounted approximately to US$2,400 per beneficiary household.
The main component was a cash transfer known as Citizen income (Ingreso ciudadano)
11
conditional on child school attendance and health check-ups. The cash transfer consisted
in a monthly benefit equivalent to Uruguayan peso (UY$) 1363 (53 US dollars6 ) independent of the number of household members7 . The amount of the transfer represented
50% of the average self-reported household income before the program. In practice, the
Citizen income covered nearly all the successful applicants of PANES (see Table 1).
The citizen income was meant to cover all successful applicants of the program, except
participants of the public work employment component (Trabajo por Uruguay). This
was a non-mandatory transitory employment program, for which successful applicants
to PANES were invited to enroll and beneficiaries were then randomly selected from
among individuals enrolled. The program consisted in a temporary work activity for one
of the household members and the beneficiary received a salary that doubled the Citizen
Income. The latter was suspended during the period of work which normally lasted six
months. This component eventually covered 20% of PANES beneficiary households.
Additionally, households with children below 18 or pregnant women received an extra
benefit (called Tarjeta alimentaria) which consisted of an in-kind transfer delivered by
means of a debit card which allowed households to purchase only food and cleaning
and health products. The transfer was monthly and varied according to the number
of children and pregnant women in the household. It ranged from 12 US$ for a single
child to a maximum of 31 US$ for more than three children. While the cash transfer
was operative since May 2005, due to logistical problems the food card did not operate
until the end of April 2006. It eventually reached 73% of PANES beneficiary households,
being the second most important component.
Other smaller components included, among others, job training and education activities,
free provision of building materials for home improvement and repairing, free health
interventions such as eye surgery, dental treatments and prostheses and facilities to get
regular connection to essential services (water and sewer) and provision of night shelter
for homeless households. The scope of these components was however limited; none of
them covered more than 20% of PANES beneficiaries.
6
7
At the April 1 2005 exchange rate.
The amount of the transfer was adjusted every four months according to the Consumer Price Index.
12
Table 1: Coverage of PANES Components (% of total beneficiaries)
Proportion of beneficiaries
(self-reporting)
Citizen income
Food card
Employment
Training and education
Other
97.4
73.0
19.6
17.1
12.4
Source: based on PANES first follow-up survey.
3.2
Program eligibility
The selection of beneficiaries was based on a proxy means tested after a self-enrollment
process that comprised two stages. On a first stage, low-income households were invited
to apply to the program providing basic information about household members and
reporting total household income. Households could apply during the whole duration
of the program. Also, the Ministry of Social Development (MIDES) in charge of the
implementation made an important e↵ort to reach very deprived households that have
failed to enrol, which led to increase applications by 12,000 households. Overall, 246,681
households applied (nearly 25% of all households).
Household eligibility was determined in accordance with two criteria. First, household
per capita income should not exceed 1300 UY$ (51 USD). Income was computed as
the maximum between self-reported income and income in social security registers
(excluding non-contributory benefits). Second, among those households whose income
was below that threshold, beneficiaries were selected using a predicted poverty index.
On the second stage of enrollment, enumerators were then sent to applicants’ houses
whose per capita monthly income did not exceed that limit. During these visits, a
baseline survey including detailed information on household characteristics (mainly
access to durable goods and housing conditions) and individual characteristics (sex, age,
education, labor market participation, income) was carried out. This information was
subsequently used to estimate a predicted poverty score for each household. At this
stage, households were not informed about the variables that would be used to determine
final eligibility to the program. Note also that the vast majority of applications took
place during 2005. This reduces the concern about whether household that apply later
on could have additional information on the eligibility criteria, leading to a potential
manipulation of the score on later stages of the program (see Figure A.1). Due to the
means tested criterion approximately 25% of applicant households were rejected and
13
eventually 188,671 households were visited.
The score is estimated as a linear combination of non-monetary household characteristics
collected in the baseline survey and it is based on a probit model of the likelihood of
belonging to the bottom quantile of poverty among poor households8 . A greater score
represents a higher predicted poverty, therefore only households whose score was above
a certain threshold were selected. Successful applicants received the cash transfer since
their inscription until the end of the program, unless their formal income exceeded the
predetermined level or misreporting in the information households provided to compute
the predicted poverty index was detected through visiting the applicants at home.
Rejected households could reapply.
The selection of the eligibility criterion responded to the fact that authorities were
committed to applying a non-discretionary assignment rule. The predicted poverty
index was elaborated by an external research team from the public national university.
A proxy means test has several advantages over income as an assignment rule. First,
income can be easily subjected to misreporting since households had incentives to
underreport it in order to get the benefits. Besides, since the informal sector is an
important source of income for many poor households in Uruguay, income cannot be
completely verified against social security records. On the contrary, the proxy means test
is based on variables that are not easily manipulated by applicants. Moreover, income of
poor households experience significant variations over short periods of time so it is not a
good approximation to permanent income (Amarante et al., 2005).
In principle, the transfers were disbursed conditional on school attendance for children
aged 6 to 14 years old and health check-ups for children below 5 and pregnant women. In
practice, however, due to inter-institutional coordination problems the conditions were
not enforced. Beneficiaries were not informed of this absence of monitoring while the
program was active, which was acknowledged by authorities only after the end of the
program. However, evidence from a 2007 follow-up survey shows that beneficiaries were
not fully aware of the existence of conditions. In particular, while 53% of beneficiary
households reported being aware that some conditions were required, barely more than
20% identified that the program was conditional on school attendance. This indicates
that the potential e↵ects of conditions on school outcomes might be limited. Thus, the
8
The variables included in the score are: indicators for public employees in the household, for retired
workers, for pensioners and for private health coverage, logarithm of household size, indicators for
presence of children below 5 and children aged 12 to 17 in the household, index of durable goods,
average years of education of adult members, indicator for overcrowding, indicators for type of sewerage
system, indicators for whether the household rents or occupies the house. Di↵erent eligibility thresholds
were determined for five regions in order to cover a similar share of poor households in each area. Details
on the methodology can be found in Amarante et al. (2005).
14
income e↵ect rather than the conditions probably played a greater role to explain any
observed e↵ect on school outcomes.
4
4.1
Empirical strategy
Methodology
We are interested in estimating the causal e↵ects of PANES on school outcomes. Being
Yi the outcome for individual i, we would ideally estimate Yi (1) Yi (0), where Yi (1)
is the potential outcome when the individual receives the benefits and Yi (0) is the
potential outcome without exposure to the program. The basic problem for estimating
the causal e↵ect is that we cannot observe the same individual in both states at the
same time. Therefore, the identification of causal e↵ect must rely on estimating average
treatment e↵ects by comparing the outcomes on groups with di↵erent treatment status.
If individuals were randomly assigned to the program we could estimate its impact
comparing average outcomes on the treated group with the corresponding average on the
control group, i.e. those individuals that did not receive the benefits but were otherwise
(in expectation) identical to the treated group.
In the case of PANES, however, assignment was determined using a predicted poverty
score and therefore only those households with a score above a certain cut-o↵ point were
eligible to the program. Accordingly, individuals that received treatment di↵er from
ineligible individuals. Nevertheless, taking advantage of the program eligibility criterion,
which leads to a quasi-experimental design, we can rely on a regression discontinuity
approach (RD) in order to identify the causal e↵ect of the program. Note that this
study will not focus on distinguishing the impact of the di↵erent components of the
program. Instead, the overall impact of PANES benefits is examined, which as stated
before comprised in most cases the Citizen Income and the food card.
The basic idea of the RD is that the assignment rule of the program, based on a cut
value of a treatment variable, provides exogenous variation in treatment status. In fact,
if individuals are unable to precisely control the assignment variable, the variation in
treatment around the cut-o↵ resembles a randomized experiment (Lee and Lemieux,
2010). This implies that individuals around the eligibility threshold are similar on
unobservable and observables characteristics and therefore those individuals just below
the cut-o↵ provide a valid counterfactual for individuals just above the cut-o↵. We can
then estimate the treatment e↵ect by comparing average outcomes for individuals on
each side of the eligibility threshold. In other words, under the assumption that the
expected potential or counterfactual outcomes are continuous in the assignment variable,
15
any discontinuity at the eligibility threshold in any outcome potentially a↵ected by the
treatment can be interpreted as the causal e↵ect of the program (Imbens and Lemieux,
2008).
A key element in the RD analysis is then the enforcement of the assignment rule. When
there is perfect enforcement of eligibility rules, treatment is solely determined by the
predicted poverty score, implying that every household with a score above the eligibility
threshold receives the program while every household with a score below the cut-o↵ does
not receive the benefits. Formally, being Ti an indicator for treatment, it holds that
Ti = Di where Di is and indicator for whether the score is above the discontinuity point
Di = 1(Si > c). In this case, known as Sharp Regression Discontinuity design (SRD),
assuming continuity of potential outcomes in the assignment variable, the average causal
e↵ect of the treatment at the eligibility threshold (c) is given by the di↵erence in the
conditional expectation of the outcome given the score9 :
⌧SRD = lim E [ Y | S = c + "]
"#0
lim E [ Y | S = c + "]
""0
Figure 3 reports the proportion of households that ever received the program benefits as
a function of their predicted poverty score. The discontinuity observed at the threshold
suggests that the assignment to the program mostly followed the technical rule. The great
majority of eligible households, i.e. those with (normalized) score above 0, received the
treatment while the opposite is true for ineligible applicants. Nevertheless, compliance
with the assignment rule was not perfect. In e↵ect, the discontinuity in the probability of
being treated at the eligibility point is 85 pp.10 When the assignment is not a deterministic
function of the score, which is known as Fuzzy RD, the average causal e↵ect of the
program is now given by the ratio of the discontinuity in the outcome on the score to the
discontinuity in the assignment variable on the score:
⌧FRD =
lim E [ Y | S = c + "]
"#0
lim E [ Y | S = c + "]
lim E [ T | S = c + "]
lim E [ T | S = c + "]
"#0
""0
""0
Basically, the identification of treatment e↵ects under FRD implies using an indicator
for whether the score is greater than the cut-o↵ (Di ) as an instrument for treatment
status (Ti ).
9
A more detailed presentation can be found for instance in Imbens and Lemieux (2008), Lee and Lemieux
(2010) and Van der Klaauw (2008).
10
Figure A.2 in Appendix reports similar results for the sample used in the follow-up survey. The
discontinuity in this case shows that compliance with the eligibility rule was almost perfect. The
conditional probability of receiving the program on the score jumps from 0 to 1 at the eligibility
threshold with a discontinuity of 99 pp. This leads to a SRD.
16
0
.2
.4
.6
.8
1
Figure 3: PANES treatment and eligibility.
−.02
−.01
0
.01
.02
Predicted poverty
Source: Based on PANES administrative records.
Note: The score is centered at zero. A linear regression on each side
of the threshold is fit to the data.
4.1.1
Estimations
As suggested by Imbens and Lemieux (2008), we can estimate the treatment e↵ect ⌧ by
running local linear regressions, i.e. a linear regression on either side of the cut-o↵ using
only observations that are close to the cut-o↵. The e↵ect can be directly estimated fitting
pooled regressions on both sides of the discontinuity point as follows:
Yi = ↵1 + ⌧1 Di +
1 (Si
c) +
1 Di (Si
c) +
0
1 Zi
+ ✏1i
(1)
Ti = ↵0 + ⌧0 Di +
0 (Si
c) +
0 Di (Si
c) +
0
0 Zi
+ ✏0i
(2)
where Si c is the predicted poverty index centered at zero, Zi represents a set of
additional covariates and ✏1i and ✏0i are error terms. Note that we allow the slope of the
regression lines to di↵er on each side of the threshold by including an interaction term
between the score and the indicator for eligibility.
Under SRD, since Di and Ti are equivalent, the e↵ect of the program is directly estimated
from (1) as ⌧ˆSRD = ⌧ˆ1 . This procedure will be implemented in section 5.1 to estimate the
e↵ect of the program on school attendance as reported in the follow-up surveys. As stated
earlier, in the sample used for these surveys the jump in the probability of treatment at
the cut-o↵ point is almost 1. However, the main results, presented in section 5.2, will be
estimated using a FRD, which corresponds to estimating the ratio ⌧ˆF RD = ⌧ˆ1 /ˆ
⌧0 . Note
that this procedure is equivalent to running two-stage least squares (2SLS) regressions
which instrument treatment by the eligibility indicator. The first stage estimates T̂i from
(2) and the second stage is equivalent to:
17
Yi = ↵1 + ⌧1 T̂i +
1 (Si
c) +
1 Di (Si
c) +
0
1 Zi
+ ✏1i
(3)
However, when the underlying function is not linear around the cut-o↵, the estimation
will be biased. Therefore, following the proposal of Porter (2003) on local polynomial
estimation we will further estimate the treatment e↵ect fitting more flexible regressions
by adding higher-order polynomial terms on the score. This procedure allows to account
for potential polynomial type behavior of the conditional expectation around the discontinuity point. Interaction terms between the polynomials and an indicator of program
eligibility are also added to allow the shape of the underlying function to di↵er in either
side of the cut-o↵11 :
Yi = ↵1 + ⌧1 Di +
1p
n
X
(Si
c)p + Di
p=1
T i = ↵ 0 + ⌧ 0 Di +
0p
n
X
n
X
1p (Si
c)p +
0
1 Zi
+ ✏1i
(4)
0p (Si
c)p +
0
0 Zi
+ ✏0i
(5)
p=1
(Si
p
c) + Di
p=1
n
X
p=1
where p represents the degree of the polynomial functions on the normalized score.
For each school outcome, I fit polynomials of order 1 (which is equivalent to a local
lineal regression) to order 5. The optimal degree of the polynomial will be chosen using
Akaike information criterion for model selection12 . Similarly to the case of local linear
regression, the FRD will be implemented by 2SLS.
The e↵ect of the program is estimated for the school year 2007, which is the closest year
to the end of the program. Therefore, the treatment population is restricted to those
households who receive the first cash payment before the end of the first trimester of
2007 and the overall population is restricted to households who receive the baseline visit
up to the end of February. Due to the non perfect compliance with the assignment rule,
the treatment variable will be instrumented using an indicator of eligible households
above the threshold who would receive the transfer before the beginning of the second
trimester. One concern on the analysis is the e↵ect of di↵erent time of exposure to the
program. Households stopped receiving the transfer when their income exceeded the
income threshold. As a consequence, those households with higher time of exposure are
probably worse-o↵ than household who receive the transfer for shorter periods since they
were able to find a job or have other positive income shocks. In order to assess this issue,
results systematically provide a specification including indicators of month of baseline
11
12
A similar strategy is followed by, among others, Lee et al. (2004) and Matsudaira (2008).
The Akaike information criterion for model selection is given by: AIC = N ln(ˆ 2 ) + 2k, where N is
the number of observations, ˆ 2 is the mean squared error of the regression and k is the number of
parameters of the regression. Given the set of model specifications, the optimal is the one with the
lowest AIC value.
18
survey and month of enrollment as proxies for time of exposure.
A relevant issue in RD estimates using local regressions is the choice of the bandwidth
which determines the size of the local neighborhood around the cut-o↵ that will be
used to estimate treatment e↵ects. The optimal bandwidth will be chosen following
the proposal of Imbens and Kalyanaraman (2009). Robustness of the findings will be
checked using several alternative bandwidths.
The validity of the design depends on the absence of manipulation of the assignment
variable by individuals. As stated earlier, a credible identification of the program e↵ect
under RD relies on the continuity of the potential outcome in the assignment variable.
However, this assumption may not hold if agents are able to precisely control the
variables that determine the score in order to be eligible to the program. Although this
concern is limited in the case of PANES, due to the enrollment process already described,
I will follow McCrary (2008) proposal in order to formally test whether manipulation
of the assignment variable might have taken place. The underlying idea is that in
the absence of manipulation the distribution of the predicted poverty score should be
continuous at the threshold. Also, the validity of the RD design can be further checked
by analyzing whether pre-treatment characteristics are smoothed in the forcing variable
at the eligibility threshold (see section 5.4).
The RD provides a highly credible identification strategy and has therefore relatively
strong internal validity. The main disadvantage however is its limited external validity.
Results are estimated only at the eligibility threshold and cannot be generalized without
additional assumptions such as constant treatment e↵ects.
4.2
Data
This study is based on two main datasets, namely the PANES official administrative
and secondary school records. Since both datasets contain the national identification
number (known as cédula) of all household members and students respectively they can
be matched.
The administrative records of the program provide baseline information on household
characteristics (mainly access to durable goods and housing conditions) and individual
characteristics (sex, age, education, labor market participation, income) both for
successful and unsuccessful applicants. It also contains the predicted poverty score
that determined eligibility for each household as well as information on whether the
household received or not the program. This information was gathered mainly between
19
2005 and 2006, although it contains some data for 2007, depending on the moment when
households asked for the benefits. This dataset allows to clearly identify whether the
student belongs to a household that received the program or not.
The second dataset used in this study are the administrative records from secondary
school in Uruguay. For the first four years of secondary school, the dataset contain
information on attendance, promotion, average qualification and cause of repetition
(poor attendance or poor academic performance). Unfortunately, there is no information
on school characteristics such as student-teacher ratio or access to learning materials.
Secondary school administrative records are available each year from 2004 to 2009. This
dataset is used to identify the impact of the program on a set of school outcomes such
as number of absences, repetition and performance. In order to assess the program
impact, data from 2007 when PANES was still active but close to its end will be used.
Also, information from 2004 allows us to check whether there were any pre-program
di↵erences in relevant outcomes between treatment and control groups.
Additionally, two follow-up surveys are used to estimate the e↵ects of the program on
reported school attendance among adolescents aged 13 to 16. The first follow-up survey
was collected between October 2006 and March 2007, approximately a year and a half
after the start of the program. The survey was purposely designed to carry out the
impact evaluation of the program and was designed by researchers at the Uruguayan
public university. The sample comprised around 3000 households with a score 4%
around the cut-o↵. The questionnaire resembled the baseline survey, including standard
information on household and individual characteristics13 . The second follow-up survey
was carried out between February and March 2008 immediately after the end of the
program. Information on households surveyed can be linked to the baseline information
provided by the program administrative records.
Table 2 displays descriptive statistics on school outcomes from the school registers prior
to the beginning of the program. Results are disaggregated considering children’s household status relative to the program. As expected, students from treatment households
present worse school characteristics in comparison to non-successful applicants and nonapplicants. In particular, they have lower average qualifications per grade and lower
attendance rates as well as higher repetition rates, although the di↵erences are relatively
small. Similarly, children are ordered according to their household characteristics (Table
A.3). Successful applicant households are characterized by a higher presence of female,
younger and less educated household heads, lower income and higher size. The di↵erences
13
The survey also included additional information: knowledge of rights, opinions and expectations and
participation in social groups.
20
with unsuccessful applicants are all significant at 99 % level.
Table 2: Pre-program descriptive statistics on school outcomes.
School
outcomes
Total
Reported school
attendance
73.012
[0.444]
Total absences
23.219
[31.314]
20.777
[31.070]
5.044
[7.682]
25.618
[0.437]
11.035
[0.313]
14.583
[0.353]
72.818
[0.445]
7.560
[1.596]
21.258
[29.161]
18.924
[28.882]
4.836
[7.421]
22.965
[0.421]
9.598
[0.295]
13.367
[0.340]
75.573
[0.430]
7.621
[1.624]
116371
84825
96165
72735
Non - applicants
PANES applicants
Successful
Unsuccessful
Dif. Successful
- Unsuccessful
Baseline survey
N/A
N/A
69.764
[0.459]
77.941
[0.415]
-8.177***
[0.004]
35.345
[40.969]
32.409
[41.003]
5.982
[8.821]
40.769
[0.491]
19.866
[0.399]
20.902
[0.407]
56.895
[0.495]
7.173
[1.336]
29.469
[35.681]
26.479
[35.667]
6.083
[8.672]
35.454
[0.478]
15.673
[0.364]
19.781
[0.398]
62.815
[0.483]
7.208
[1.374]
5.876***
[0.543]
5.930***
[0.543]
-0.102
[0.123]
5.315***
[0.007]
4.194***
[0.005]
1.121**
[0.006]
-5.920***
[0.007]
-0.034
[0.025]
10616
6054
9590
6036
Secondary school registers
Unjustified absences
Justified absences
Repetition
Rep. due to absence
Rep. due to performance
Promotion
GPA
Observations
Observations(GPA)
Standard deviations between brackets.
5
Results
The following section comprises two main separate parts. The first analyzes whether
the program increased school attendance considering adolescents both inside and outside
school. As shown below, these results provide evidence in favor of the validity of the
identification strategy used in the second part, which analyzes the e↵ect of PANES on a
ample set of school outcomes observed only for students enrolled at secondary school.
5.1
Impact on reported school attendance
Using data from the first and second follow-up surveys, which surveyed successful and
unsuccessful applicants to the program, we can estimate the e↵ect of PANES on the
proportion of children that report being attending school at the moment of the survey.
While the measure is a raw approximation to school attendance, it allows to estimate
the e↵ect on the whole population in school age. Thus, it does not su↵er from selection
bias which might a↵ect school registers that contain information exclusively on students
that are enrolled at school. Consequently, the analysis on reported school attendance
21
provides insight into the potential bias that may a↵ect the identification of treatment
e↵ects on school outcomes using school registers.
Follow-up surveys yield, however, an imprecise measure of school attendance. First,
reported attendance does not provide information on how often children attend school
and there is no other information on these surveys that can be exploited to assess
the frequency of school attendance14 . Besides, there might be some concerns about
the reliability of the reported information as a measure of actual school attendance.
Although households were not informed about the purpose of the surveys, it is likely that
parents tend to overreport the attendance status of children and adolescents considering
the compulsory school attendance requirements. Also, adult respondents might not be
fully aware of children attendance status, especially at high school level, which may lead
them to answer in terms of school enrollment rather than attendance. Nevertheless, since
these concerns a↵ect both successful and unsuccessful applicants the information can
be used to assess whether the program increased the proportion of children attending
school. Note also that reported school attendance among successful applicants before
the program amounts to 70%, considerably below the maximum (see Table 2).
For the sake of comparability with school records, the analysis on school attendance
is restricted to children aged 13 to 16, which in theory should be attending grades
one to four of high school. Note, however, that due to repetition, which tend to
be particularly high among poor children, both groups do not necessarily coincide.
Nevertheless, since the goal is to analyze the e↵ect of the program for all children, regardless of their attendance status, we cannot consider information on school grade which
is only available for those who report being attending school at the moment of the survey.
Table 3 reports estimates of the e↵ect of PANES on reported school attendance for
both surveys. The graphical analysis is presented in the Appendix. Treatment e↵ects
are estimated by local regressions including polynomial terms of degree one and two.
As stated earlier, the optimal specification of the model was chosen using the Akaike
information criterion among five specification including polynomials of degree one to
five. The Akaike criterion suggested a local linear regression for school attendance in
the first follow-up survey and a third-degree polynomial for the second follow-up survey
(Table A.4 in the Appendix). The following regressions report polynomials of orders
one and two. Table A.6 additionally reports a third-degree polynomial for the second
survey in order to check robustness of the results to the optimal specification selected by
Akaike.
14
The first follow-up survey includes information on frequency of absences but the responses have extremely low variance to be considered.
22
Results show that the program did not a↵ect the proportion of children who were
attending school at the time of each survey. The absence of impact is robust to di↵erent
specifications that include children control variables (age and gender), household
variables (age, gender and education of household head, income and household size) and
regional dummies. Table A.5 reports additional specifications including extra control
variables (occupation status of household head and roof and ceiling materials) but no
significant di↵erences are observed.
Even when there is weak evidence of a positive e↵ect in the first follow-up survey for the
specification including a second-degree polynomial and child characteristics, the e↵ect
vanishes when adding household control variables. Also, there is no robust evidence of
an increase on school attendance when the analysis is disaggregated by gender of the
child15 . The results are similar to those found in Amarante et al. (2011a). This lack of a
substantial positive e↵ect on school attendance may be explained by the fact that most
households were not aware of the school conditionalities or that the income e↵ect did
not fully operate.
The absence of program e↵ects on the proportion of beneficiary children that attend
school tends to limit the potential concern on selection bias that may arise when school
outcomes are only available for those students who are enrolled at school. If a program
has an e↵ect on school enrollment, it may foster attendance among children who are
poorer than those already attending. Children already attending school are probably
more motivated than those who were out of school before the program, for example
because they have unobservable characteristics that increase their (perceived) returns on
schooling. As a consequence, children brought to school by the program will tend to
perform worse at school. This may lead to a misleading identification of the program
e↵ect. Since the program did not increase the proportion of children attending school
it allows to analyze whether it had any impact on school outcomes for those who are
enrolled at school.
15
There is some weak evidence of a positive impact for girls in the first follow-up survey but the e↵ect
is only significant for two-degree polynomial specifications which are not the optimal ones.
23
Table 3: Program e↵ect in reported school attendance. Follow-up surveys.
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
0.104
[0.077]
703
0.130
[0.107]
332
0.055
[0.092]
371
0.172
[0.113]
703
0.277⇤
[0.151]
332
0.030
[0.141]
371
0.103
[0.077]
703
0.121
[0.105]
332
0.067
[0.093]
371
0.166
[0.114]
703
0.258⇤
[0.154]
332
0.054
[0.144]
371
First follow-up survey
All
Observations
Girls
Observations
Boys
Observations
0.093
[0.079]
729
0.113
[0.109]
342
0.078
[0.104]
385
0.187
[0.116]
729
0.248
[0.157]
342
0.131
[0.165]
385
0.106
[0.074]
727
0.108
[0.105]
342
0.104
[0.089]
385
0.179*
[0.108]
727
0.226
[0.146]
342
0.117
[0.136]
385
Second follow-up survey
All
Observations
Girls
Observations
Boys
Observations
Child controls
Household controls
Regional controls
0.041
[0.053]
691
0.056
[0.068]
335
0.027
[0.084]
356
-0.079
[0.091]
691
0.003
[0.114]
335
-0.167
[0.150]
356
0.048
[0.051]
691
0.064
[0.065]
335
0.026
[0.081]
356
-0.042
[0.082]
691
0.019
[0.105]
335
-0.116
[0.140]
356
0.026
[0.052]
671
0.074
[0.069]
327
-0.033
[0.082]
344
-0.080
[0.083]
671
0.021
[0.110]
327
-0.181
[0.141]
344
0.037
[0.053]
671
0.090
[0.069]
327
-0.019
[0.083]
344
-0.064
[0.084]
671
0.048
[0.111]
327
-0.144
[0.143]
344
No
No
No
No
No
No
Yes
No
No
Yes
No
No
Yes
Yes
No
Yes
Yes
No
Yes
Yes
Yes
Yes
Yes
Yes
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: Odd columns include polynomial expressions on the score of degree 1 and even columns include
polynomial of degree 2. Columns (3) and (4) control for children characteristics: gender and age.
Columns (5) and (6) include additional controls on pre-treatment household characteristics: gender,
age and years of education of household head, logarithm of pre-program income per capita and
household size. Columns (7) and (8) additionally include indicators for administrative regions.
5.2
Impact on school outcomes
Table 4 displays the e↵ects of PANES on a set of school outcomes reported in secondary school registers for children who were enrolled at school in 2007. The records
have individual information on number of justified and unjustified absences from
school, and child promotion or repetition status disaggregated by cause of repetition16 .
Also, for those who were promoted, school registers report information on average score17 .
Regressions on this section consider children from households with a score 10% around
each side of the cut-o↵ and include one and two degree polynomials. The bandwidth
was selected applying the procedure suggested by Imbens and Kalyanaraman (2009)
16
Note that repetition and promotion are not exhaustive conditions since there is a small group of
students who where neither promoted nor repeaters. These students can be categorized as partial
promotion; they are allowed to enter in the following grade but have not yet finished the current grade
Results on partial promotion are not presented since the group is small.
17
A description of each of the school outcomes is available in Table A.1.
24
to a local linear regression on the outcome18 . As suggested by Imbens and Lemieux
(2008), same bandwidth is used in the regressions for outcome and treatment variables.
Results suggested an optimal bandwidth ranging from 7 to 12% depending on the school
outcome (Table A.7). Therefore, main results use a window width of 10% and then
robustness checks to di↵erent bandwidths are performed.
The degree of the polynomial was again chosen using the Akaike information criterion.
For each of the outcomes, regressions were estimated including polynomial terms (alone
and interacting with the eligibility indicator) of order 1 to 5. The model selection
procedure using a bandwidth of 10% suggested a polynomial of order 1 or 2 for all
outcomes, with the exception of repetition for which a four-degree polynomial was
suggested. For sake of simplicity, all regressions with a bandwidth of 10% include up to
two-degree polynomials.
Results show di↵erential impacts among the set of school outcomes. There is evidence of
a reduction on unjustified absences due to the program, which is always statistically significant at 95 or 90% level of significance. This result is robust to di↵erent specifications
including child and household covariates as well as one and two degree polynomials.
PANES led children from beneficiary households to attend between 3 and 5 extra days
along the school year. Since the school year last approximately 9 months in Uruguay,
absences are reduced by roughly 0.5 days a month. Results are similar to those found
for the program PATH in Jamaica (Levy and Ohls, 2007).
Considering that school year comprises in principle 155 days, the e↵ect may seem limited
in terms of the time children spend at school. However, taking into account that a
student cannot exceed 20 unjustified absences a year, the e↵ect may be relevant for
those children with risk of repetition due to poor attendance. Besides, if we consider
the pre-treatment number of absences among children from beneficiary households, the
e↵ect represents a considerable reduction in school absenteeism ranging from 9 to 15%.
On the other hand, the e↵ect must be analyzed in the context of pre-treatment school
outcomes in Uruguay. A relevant issue is how much room PANES had to a↵ect school
attendance. If we make a conservative estimate and consider the maximum potential
length of a school year (155 days), pre-treatment attendance rates were just below 80%
among beneficiaries, so we can conclude that there was some room for improvement.
Results also show that PANES had no significant impact on justified absences. Consequently, the negative e↵ect observed in total absences is solely explained by the reduction
on unjustified absences. These results suggest that the program led poor children to
18
The selection was implemented using the stata command rd developed by Nichols (2011).
25
spend more time at school per se and not through a reduction on causes such as illness
that may prevent students from attending school. This evidence contrasts with results
in the previous section, which did not find any e↵ect on school participation among all
PANES beneficiaries. A plausible explanation for these apparently contradictory results
might be that the transfer was not enough to incentive children already outside school
to re-enter and attend regularly. However, it seems more likely that the program have
promoted higher attendance among those already attending school.
Due to a reduction in absence we could expect a reduction on repetition since students
might now comply with the minimum requirement on attendance in order to be
promoted. There is some evidence that the small increase on attendance due to PANES
led to a reduction on repetition due to poor attendance, but the e↵ect is negligible
and not robust to all specifications. Since children around the eligibility threshold
belong to poor households, they are likely to have a low rate of attendance and thus
a high rate of repetition due to poor attendance. Therefore, the magnitude of the impact on school attendance was probably too small to substantially reduce repetition rates.
Finally, there is no evidence that PANES significantly a↵ect any other school outcome,
although coefficients have in general the expected sign. In particular, there is no e↵ect
on promotion or average qualification per grade. Note however that grade point average
(GPA) data is only available for non-repeaters and then the results are conditional on
being promoted.
To check the robustness of the results, Table A.5 reports two additional specifications
including extra pre-treatment household characteristics (occupational status of household
head and house materials of roof and floor) as well as indicators for a more disaggregated
regional variable (known as localidad ). There are no significant di↵erences with the main
results. Apart from the inclusion of a wide set of covariates, robustness of the findings is
checked using di↵erent bandwidths.
Table A.11 includes treatment e↵ects using observations with a predicted score on a
surrounding of 6 % of the cut-o↵, which is just below the minimum optimal bandwidth
among all outcomes (for unjustified absences). Note that using a smaller bandwidth
reduces the potential bias of the results although it may lead to imprecise estimates
due to higher variance (Lee and Lemieux, 2010). According to the optimal order of
the polynomial selected by Akaike (see Table A.10), all regressions include a one-degree
polynomial and same controls as Table 4. Results on unjustified absences are consistent
to the ones found using a bandwidth of 10% but the weak e↵ect on repetition due to
poor attendance disappears.
26
Table 4: Program e↵ect in school outcomes. 2007
Total absences
Unjustified absences
Justified absences
Repetition
Rep. due to attendance
Rep. due to performance
Promotion
GPA
Observations (GPA)
Observations
Child controls
Household controls
Regional controls
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
-2.772
[1.686]
-2.991⇤
[1.681]
0.245
[0.414]
-0.030
[0.021]
-0.040⇤⇤
[0.018]
0.009
[0.016]
0.026
[0.021]
-0.010
[0.076]
-5.095⇤⇤
[2.525]
-4.999⇤⇤
[2.517]
-0.253
[0.624]
-0.045
[0.032]
-0.032
[0.027]
-0.013
[0.024]
0.047
[0.032]
0.099
[0.117]
-3.068⇤
[1.616]
-3.284⇤⇤
[1.614]
0.242
[0.411]
-0.033
[0.020]
-0.041⇤⇤
[0.017]
0.008
[0.016]
0.029
[0.020]
-0.001
[0.075]
-5.360⇤⇤
[2.412]
-5.263⇤⇤
[2.411]
-0.253
[0.617]
-0.048
[0.030]
-0.035
[0.026]
-0.013
[0.024]
0.052⇤
[0.030]
0.119
[0.115]
-2.901⇤
[1.619]
-3.041⇤
[1.616]
0.113
[0.417]
-0.030
[0.020]
-0.040⇤⇤
[0.017]
0.009
[0.016]
0.028
[0.020]
0.000
[0.076]
-5.366⇤⇤
[2.391]
-5.222⇤⇤
[2.390]
-0.322
[0.627]
-0.046
[0.030]
-0.035
[0.026]
-0.010
[0.024]
0.050
[0.031]
0.126
[0.116]
-2.757⇤
[1.625]
-2.795⇤
[1.625]
-0.065
[0.416]
-0.038⇤
[0.020]
-0.039⇤⇤
[0.017]
0.001
[0.016]
0.036⇤
[0.020]
0.022
[0.075]
-4.966⇤⇤
[2.390]
-4.924⇤⇤
[2.391]
-0.151
[0.627]
-0.042
[0.030]
-0.030
[0.026]
-0.011
[0.024]
0.045
[0.031]
0.124
[0.114]
8063
13238
8063
13238
8063
13238
8063
13238
7894
12942
7894
12942
7894
12942
7894
12942
No
No
No
No
No
No
Yes
No
No
Yes
No
No
Yes
Yes
No
Yes
Yes
No
Yes
Yes
Yes
Yes
Yes
Yes
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: Odd columns include polynomial expressions on the score of grade 1 and even of order 2. Columns (3) and (4)
include children characteristics: gender and age of child, grade and curricula. Columns (5) and (6) additionally include
household characteristics: gender, age and years of education of household head, variables for household composition
and logarithm of pre-program income per capita. Columns (7) and (8) additionally include dummies for administrative
regions, month of enrollment and month of baseline survey.
Further checks assess treatment e↵ects using larger bandwidth up to 20%. Table A.12
displays results using 15% of observations around the discontinuity point and including
a second order polynomial terms (see Table A.10). Results using a window of 15% are
highly consistent with those using a 10% bandwidth. In particular, the negative e↵ects
on total absences (driven by unjustified ones) and repetition (driven by repetition due
to absences) are significant in the four specifications19 . In sum, the overall results tend
to be consistent with di↵erent specifications that control for a wide set of covariates and
are robust to di↵erent bandwidths.
5.2.1
Heterogeneity e↵ects
This section analyzes whether the program had a di↵erential impact among di↵erent
subgroups. Table 5 reports results on school outcomes disaggregated by gender. Sur19
Finally, using a 20 % bandwidth the negative e↵ect on unjustified absences does not hold for specifications with a two-degree polynomial (see Table A.13). Note however, that this may respond to a
composition e↵ect since treatment and control groups further away from the cut-o↵ tend to increasingly
di↵er.
27
prisingly, the e↵ects are markedly di↵erent between both groups. In e↵ect, the impact
on attendance observed for the whole population is solely explained by the reduction of
absenteeism among girls whereas boys did not experience any substantial change in their
school performance due to PANES. The e↵ect on unjustified school absences among girls
varies from 5 to 8 absences a year and represents a reduction from nearly 20% to 30%
with respect to pre-treatment levels (see Table A.2). This e↵ect amounts to a reduction
in monthly absenteeism ranging from roughly 0.6 to 0.9 days a month. The e↵ect on
unjustified absences is robust to di↵erent specifications adding multiple control variables,
using a range of bandwidths and including di↵erent orders to the polynomial. In short,
we observe that PANES led girls to spend more time on school.
Notice that prior to the program boys perform worse than girls, which would indicate
that there was more room to a↵ect school attendance among the former (see Table A.2).
However, CCTs program, as is the case of PANES, give transfers in general to women,
which may increase their decision-making power in the household. There is evidence
that individual’s preferences over consumption di↵ers between women and men (Doss,
2006; Ward-Batts, 2008). In particular, studies have found in general a higher impact
of cash transfers on children outcomes when the transfers are targeted to adult women.
Besides, although the findings are not conclusive, there is some evidence that the e↵ect
tend to be higher among female children (see for instance Barrientos and DeJong (2006)
and Aslam (2007)).
Similar to other CCTs, PANES gives transfers mainly to women and 75 % of PANES
recipients are indeed women. Unfortunately, there is not a clear strategy that might
allow to disentangle the causes for this gender-biased e↵ect of the program. Therefore,
even while PANES favors women as recipients of the transfers, whether this channel
operated remains an open question.
28
Table 5: Program e↵ect in school outcomes by gender. Bandwidth 10%. 2007
Girls
Total absences
Unjustified absences
Justified absences
Repetition
Rep. due to attendance
Rep. due to performance
Promotion
GPA
Observations
Child controls
Household controls
Regional controls
Boys
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
-5.167⇤⇤⇤
[1.985]
-5.519⇤⇤⇤
[1.969]
0.571
[0.554]
-0.049⇤
[0.026]
-0.060⇤⇤⇤
[0.021]
0.010
[0.019]
0.050⇤
[0.026]
0.039
[0.097]
-7.799⇤⇤⇤
[2.923]
-8.066⇤⇤⇤
[2.898]
0.418
[0.841]
-0.062
[0.039]
-0.052⇤
[0.031]
-0.010
[0.029]
0.062
[0.039]
0.155
[0.144]
-5.035⇤⇤⇤
[1.915]
-5.157⇤⇤⇤
[1.909]
0.144
[0.557]
-0.052⇤⇤
[0.025]
-0.054⇤⇤⇤
[0.020]
0.002
[0.019]
0.055⇤⇤
[0.026]
0.049
[0.095]
-8.044⇤⇤⇤
[2.773]
-8.309⇤⇤⇤
[2.760]
0.436
[0.844]
-0.061
[0.037]
-0.052⇤
[0.030]
-0.009
[0.029]
0.063⇤
[0.038]
0.190
[0.140]
0.191
[2.807]
0.134
[2.810]
-0.154
[0.584]
-0.010
[0.033]
-0.016
[0.029]
0.006
[0.027]
-0.001
[0.033]
-0.088
[0.116]
-1.610
[4.321]
-1.015
[4.327]
-1.178
[0.852]
-0.025
[0.051]
-0.008
[0.045]
-0.018
[0.042]
0.030
[0.051]
-0.008
[0.188]
0.231
[2.733]
0.310
[2.742]
-0.348
[0.587]
-0.021
[0.032]
-0.021
[0.029]
0.001
[0.027]
0.013
[0.032]
-0.021
[0.116]
-0.680
[4.124]
-0.136
[4.134]
-1.116
[0.857]
-0.014
[0.049]
-0.002
[0.044]
-0.012
[0.042]
0.020
[0.049]
0.027
[0.188]
4915
4915
4810
4810
3148
3148
3084
3084
No
No
No
Yes
No
No
Yes
Yes
No
Yes
Yes
Yes
No
No
No
Yes
No
No
Yes
Yes
No
Yes
Yes
Yes
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: All columns include polynomial terms of order 1. Columns (2) and (6) include children characteristics: age
of child, grade and curricula. Columns (3) and (7) additionally include household characteristics: gender, age and
years of education of household head, variables for household composition and logarithm of pre-program income per
capita. Columns (4) and (8) additionally include dummies for administrative regions, month of enrollment and month
of baseline survey.
Finally, e↵ects might di↵er throughout secondary school grades. Separate regressions
were run for one to four school grades (Table 6). Results show that the e↵ects are
highly concentrated in few years. On one hand, the increase on school attendance
is only significant among first graders, and is the only robust e↵ect along all school
outcomes and school grades. This result goes in line with several studies that highlight
the relevance of cash transfer to explain school behavioral changes among transitional
children from primary to lower secondary school. For instance, evaluations for Mexico,
Ecuador and Cambodia show that the largest e↵ect on school outcomes are among
children making the transition form primary to secondary school (see Schultz (2004);
Schady and Araujo (2008); Fiszbein and Schady (2009)). This is an important result
since it has been previously acknowledge that the Uruguayan educational system faces
difficulties to smooth children’s transitions from primary to secondary school.
On the other hand, there is some weak evidence of a reduction on repetition due to
absences in four grade, although there is no significant e↵ect on number of absences,
which casts doubts on the robustness of these results. Note that an e↵ect in fourth grade
attendance rates would be relevant since this is the grade of transition from lower to
29
upper secondary school and attendance rates are substantially reduced with respect to
the last year of compulsory school (third grade until 2009).
Table 6: Program e↵ect in school outcomes by grade. Bandwidth 10%. 2007
Grade 1
Total Absences
Unjustified absences
Repetition
Rep. due to attendance
Observations
Child controls
Household controls
Regional controls
Grade 2
Grade 3
Grade 4
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
-5.382⇤⇤
[2.706]
-5.702⇤⇤
[2.703]
-0.029
[0.033]
-0.042
[0.028]
-6.318⇤⇤⇤
[2.448]
-6.364⇤⇤⇤
[2.451]
-0.050
[0.031]
-0.052⇤⇤
[0.026]
-0.484
[3.227]
-0.512
[3.195]
-0.020
[0.039]
-0.033
[0.033]
1.562
[2.966]
1.489
[2.945]
0.002
[0.037]
-0.015
[0.032]
0.555
[3.566]
0.132
[3.553]
-0.013
[0.044]
-0.013
[0.035]
0.746
[3.560]
0.439
[3.555]
-0.026
[0.044]
0.000
[0.034]
-4.798
[3.983]
-4.706
[4.034]
-0.075
[0.055]
-0.086⇤
[0.048]
-5.764
[4.035]
-5.677
[4.089]
-0.093⇤
[0.055]
-0.101⇤⇤
[0.048]
4899
4899
3508
3508
2811
2811
1729
1729
No
No
No
Yes
Yes
Yes
No
No
No
Yes
Yes
Yes
No
No
No
Yes
Yes
Yes
No
No
No
Yes
Yes
Yes
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: All columns include polynomial terms of order 1. Columns (2), (4), (6) and (8) include same controls as
Columns (7) and (8) in Table 4 (except from grade).
5.3
Potential cash transfer mechanisms
As previously reviewed, the literature indicates two main potential mechanisms
through which a conditional cash transfer may a↵ect school outcomes; the potential
net income increase and the conditions attached to the program may foster school
attendance as well as higher performance among students. This section presents evidence on the potential role that both mechanisms may have played in the case of PANES.
First, the role of conditions can be exploited using information from the first follow-up
survey that asked households members whether they were aware of school conditions.
This allows to estimate whether there were some e↵ect among conditioned households on
school attendance. Table 7 presents results on reported school attendance restricting the
analysis to children belonging to conditioned households relatively to those belonging
to ineligible households. Note however, that this strategy has some shortcomings.
First, from the information available it cannot be concluded whether households were
aware of the absence of monitoring of conditions. Second, it seems plausible that
those households who were aware of conditions have distinctive characteristics from
unconditioned households, which may introduce bias in the analysis. These problems
aside, results do not show any significant impact on reported school participation among
conditioned households.
30
Table 7: Program e↵ect in school attendance for conditioned households.
First follow-up survey.
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
0.079
[0.105]
0.230
[0.155]
0.078
[0.099]
0.183
[0.149]
0.088
[0.100]
0.197
[0.152]
0.123
[0.102]
0.249
[0.154]
Observations
385
385
385
385
376
376
376
376
Child controls
Household controls
Regional controls
No
No
No
No
No
No
Yes
No
No
Yes
No
No
Yes
Yes
No
Yes
Yes
No
Yes
Yes
Yes
Yes
Yes
Yes
School attendance
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: Odd columns include polynomial expressions on the score of degree 1 and even columns include
polynomial of degree 2. Same controls as Table 3.
Second, information from social security records allows to estimate the e↵ect of the
program on total household income and household labor income for treated students who
were enrolled in school in 2007. Social security records contain individual information
on formal labor income for individuals above 14 and information on social benefits from
multiple sources including contributory and non contributory social transfers20 . Since we
want to analyze the mechanisms that might have a↵ected school outcomes as measured
at the end of the program, income measures include only payments received throughout
2007.
There is some weak evidence that PANES households had lower earnings from the
formal labor market, but the e↵ect is negligible, amounting to half a dollar a month
(Table 8). This result suggests that the program did not lead to a significant disincentive
e↵ect among adult household members. Moreover, the program lead to a relatively
high increase in total household income among beneficiaries by nearly UY$ 800 or
approximately U$S 30. As a rough approximation, considering the pre-program reported
income, this e↵ect represents an increase of nearly 30% on beneficiaries household
income. These results suggest then that the pure income e↵ect associated to the program
was not counterbalanced by a reduction in labor supply. Therefore, the general absence
of substantial impacts on school outcomes cannot be attached to the absence of a net
income increase among beneficiaries.
In summary, while the analysis on the role of conditions does not allow us to draw firm
conclusions, considering that only a relatively small proportion of beneficiaries were aware
of the conditions, the observed reduction on unjustified absences is probably explained
by the net increase on household income.
20
The main sources of income included are unemployment benefits, maternity allowances, pensions and
retirement and family allowances.
31
Table 8: Program e↵ect in household income sources. 2007
Household labor
income (formal)
Total household
income
Observations
Child controls
Household controls
Regional controls
(1)
(2)
-7.541
[5.123]
793.976⇤⇤⇤
[21.107]
-12.522⇤
(3)
(4)
[6.903]
739.213⇤⇤⇤
[32.775]
-8.222
[5.066]
793.313⇤⇤⇤
[21.094]
-13.637⇤⇤
(5)
(6)
(7)
(8)
[6.916]
738.448⇤⇤⇤
[32.770]
-7.504
[5.095]
795.851⇤⇤⇤
[21.360]
-14.106⇤⇤
[7.073]
742.908⇤⇤⇤
[33.001]
-6.618
[5.142]
788.271⇤⇤⇤
[21.187]
-14.284⇤⇤
[6.931]
750.821⇤⇤⇤
[32.623]
13250
13250
No
No
No
No
No
No
13250
13250
12950
12950
12950
12950
Yes
No
No
Yes
No
No
Yes
Yes
No
Yes
Yes
No
Yes
Yes
Yes
Yes
Yes
Yes
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Odd columns include polynomial expressions on the score of grade 1 and even of order 2. Same controls as Table 4.
5.4
Specification tests
As stated earlier, the validity of the identification strategy under RD relies on a local
random assignment to treatment. Accordingly, population on either side close to the
cut-o↵ should be similar in pre-treatment characteristics. However, a potential concern
with the implementation of the program is whether households were able to manipulate
the assignment variable in order to get the benefits. Although it was public knowledge
that eligibility would be determined by a score, this concern is reduced here since
households were not informed about the exact variables or weights to be used in its
computation. Formally, one natural alternative to analyze the validity of the design is to
check whether the conditional expectation of pre-treatment covariates are smooth on the
predicted poverty score around the discontinuity point. If the variables were manipulated
in order to a↵ect household eligibility, then we should observe a discontinuity at the
eligibility threshold.
Table 9 reports the results for a set of household pre-treatment characteristics measured
at the baseline survey. The analysis is based on those students that are recorded in
secondary registers in 2007 and whose school outcomes were analyzed in the previous
section. Evidence supports the validity of the identification strategy. Precisely, there are
no significant di↵erences among barely eligible and barely ineligible households prior to
the program in any of the following pre-treatment characteristics: logarithm of income
per capita, average years of education, household size and characteristics of household
head.
32
Table 9: Pre-treatment household characteristics on
predicted poverty score.
Outcome
Coefficient [s.e]
Observations
0.027
[0.044]
-0.049
[0.185]
1.225
[1.971]
0.028
[0.083]
0.068
[0.474]
0.048
[0.474]
17711
Ln of income per capita
Household size
Age of household head
Gender of household head
Years of education household head
Average years of education of adults
18497
18497
18497
17852
18195
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: Polynomial expressions on the score of grade 1.
Similarly, we can check whether prior to the program school outcomes display any discontinuity in the eligibility threshold that might invalidate the analysis. First, using
information from the baseline survey, Table 10 shows the results from local linear regressions of reported school attendance prior to the program on the eligibility score. The
sample is restricted to those children belonging to households that eventually were surveyed in any of the follow-up surveys. There is no evidence of discontinuities around the
eligibility threshold on reported school attendance.
Table 10: Pre-treatment reported school attendance on predicted poverty
score
School attendance
Observations
Child controls
Household controls
Regional controls
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
0.044
[0.064]
711
0.101
[0.100]
711
0.041
[0.062]
711
0.071
[0.099]
711
0.076
[0.063]
682
0.133
[0.099]
682
0.065
[0.062]
682
0.118
[0.098]
682
No
No
No
No
No
No
Yes
No
No
Yes
No
No
Yes
Yes
No
Yes
Yes
No
Yes
Yes
Yes
Yes
Yes
Yes
⇤ , ⇤⇤ , ⇤⇤⇤
significant at 90, 95 and 99% levels respectively.
Note: Odd columns include polynomial expressions on the score of degree 1 and even columns include
polynomial of degree 2. Same controls as Table 3.
For the wide set of school outcomes included in secondary registers, there is no information
available in the baseline survey. Therefore, the analysis on pre-treatment characteristics
is done using the secondary register for year 2004 which includes all students that were
enrolled at that time. Note that since the school registers are not a balanced panel, this
population is not equivalent to the group of students evaluated in section 5.2. However,
the analysis on school outcomes for 2004, before the program started, provides a useful
tool to assess whether children that eventually become PANES participants or unsuccess33
ful applicants show any discontinuity in school outcomes. In that case, the e↵ects found
in 2007 could not be exclusively assigned to the program. Results are presented in Table
11. There is also no evidence of significant di↵erences on any of the school outcomes
between barely eligible and barely ineligible children prior to the program.
Table 11: Pre-treatment school outcomes on predicted poverty score. 2004
Total absences
Unjustified absences
Justified absences
Repetition
Rep. due to attendance
Rep. due to performance
Promotion
GPA
Observations
Observations (GPA)
Child controls
Household controls
Regional controls
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
-0.209
[1.708]
-0.261
[1.697]
0.244
[0.394]
0.003
[0.021]
0.006
[0.017]
-0.002
[0.017]
0.001
[0.022]
0.131⇤
[0.077]
-0.222
[2.599]
0.278
[2.581]
-0.715
[0.593]
0.005
[0.032]
0.027
[0.025]
-0.021
[0.026]
0.010
[0.033]
0.266⇤⇤
[0.117]
1.234
[1.585]
1.115
[1.583]
0.361
[0.390]
0.017
[0.020]
0.014
[0.016]
0.003
[0.017]
-0.015
[0.020]
0.088
[0.075]
0.922
[2.435]
1.361
[2.430]
-0.603
[0.588]
0.017
[0.031]
0.034
[0.024]
-0.017
[0.026]
-0.002
[0.031]
0.229⇤⇤
[0.114]
0.941
[1.600]
0.823
[1.598]
0.342
[0.397]
0.014
[0.020]
0.010
[0.016]
0.004
[0.017]
-0.010
[0.020]
0.083
[0.076]
1.163
[2.451]
1.567
[2.445]
-0.596
[0.596]
0.016
[0.031]
0.031
[0.024]
-0.015
[0.026]
-0.003
[0.031]
0.187
[0.114]
0.737
[1.583]
0.625
[1.582]
0.363
[0.392]
0.001
[0.020]
0.011
[0.016]
-0.009
[0.017]
0.004
[0.020]
0.101
[0.075]
1.352
[2.443]
1.733
[2.440]
-0.563
[0.598]
0.023
[0.030]
0.032
[0.024]
-0.009
[0.025]
-0.011
[0.031]
0.151
[0.113]
11999
7672
11999
7672
11999
7672
11999
7672
11682
7480
11682
7480
11682
7480
11682
7480
No
No
No
No
No
No
Yes
No
No
Yes
No
No
Yes
Yes
No
Yes
Yes
No
Yes
Yes
Yes
Yes
Yes
Yes
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: Odd columns include polynomial expressions on the score of grade 1 and even of order 2. Same controls
as Table 4.
Finally, we can further check the validity of the RD design following McCrary (2008)
who provides a formal test for potential manipulation of the assignment variable. If
households (or enumerators) could manipulate the score in order to get the benefits,
we should observe a discontinuity at the cut-o↵, with a high number of households just
above the threshold (see section 4.1.1). Figure 4 reports a histogram of the number
of households according to their score and a local linear estimation of the density
on either side of the cut-o↵21 . There is no sign of discontinuity close to the score
threshold. Besides, the null hypothesis of continuity is not rejected at the 99% significance level. In conclusion, there is robust evidence to validate the identification strategy.
21
The binsize and bandwidth chosen are 0.0008 and 0.02 respectively.
34
0
2
4
6
8
10
Figure 4: McCrary’s density test on score
−.1
−.05
0
.05
.1
Note: The score is centered to zero henceforth. A predicted poverty
income higher than zero implies eligibility.
6
Conclusions
This study investigates the impact of a cash transfer in a wide set of school outcomes
using data from school registers and administrative records of the program. PANES was
an anti-poverty program carried out in Uruguay from 2005 to 2007 and was targeted to
the bottom quantile among poor households.
Results indicate the program had a modest impact on school absenteeism. Children
whose households were PANES beneficiaries attend between 3 to 5 extra days to school
relative to ineligible students during 2007. Considering the pre-treatment absences
among children from beneficiary households, the e↵ect represents a reduction of around
10%. The e↵ect is only significant for girls and first graders. If we concentrate on the
e↵ects on girls, we observe that the e↵ect on school absences, which ranges from 5 to
8 unjustified absences a year, implies a reduction of roughly 20% with respect to pretreatment levels. The e↵ect on unjustified absences is robust to di↵erent specifications
adding multiple control variables, using a range of bandwidths and including di↵erent
orders to the polynomial.
The analysis on the potential underlying mechanisms that could explain the observed
impact on attendance allows us to conclude that in the case of PANES, whose main
component was an unconditioned cash transfer, the role played by income was likely
higher than the role of conditions. Evidence on a positive net increase on household
income supports this conclusion. In terms of design of the program, these results contrast
with previous evidence that has in general highlighted the relevance of conditions to
35
explain improvements in school outcomes.
There is also some weak evidence of a reduction on repetition due to absences but
the e↵ect is not robust to di↵erent specifications. The rest of school outcomes did
not experience any substantial change due to PANES. This might point out that cash
transfers alone are not enough to foster substantial changes on school outcomes. Also,
it might indicate that in order to a↵ect school outcomes the program should be more
carefully design, for instance, monitoring conditions.
In short, we observe that PANES was e↵ective in fostering school attendance among
beneficiaries. However, the program only fostered school attendance among girls and
first graders. Besides, PANES did not a↵ect other school outcomes such as promotion or
qualification per grade. Therefore, we can conclude that even when increasing the time
children spend at school was per se a goal in the design of the program, PANES did not
lead to better school performance in terms of promotion and grading which are ultimate
goals in terms of human capital accumulation.
Results on school attendance contrast with findings from the follow-up surveys, which
show no significant impact on the proportion of children who report being attending
school. A possible explanation for this di↵erence can be attributed to the fact that children inside and out of school require di↵erent tools to incentive their school attendance.
On the other hand, it might point out to the relevance of having precise information on
frequency of school attendance.
This study raises some questions for further research. In 2008, PANES was replaced by a
more standard conditional cash transfer program which provides benefits exclusively to
eligible households with children below 18. The benefits are also conditional on children’s
school attendance for those aged 6 to 17 and health checks-ups but, contrary to PANES,
they are actually being monitored. Accordingly, it would be interesting to see whether
the impacts on school attendance di↵er once conditions are fully enforced. Also, the new
CCT will allow to analyze whether there are di↵erential impacts when the amount of the
transfer is not independent of the household size but varies with the number of school
children. Last, the new program might be useful to analyze whether the di↵erential
impact by gender still holds and to further explore the potential mechanisms underlying
these di↵erences.
36
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42
Appendix
Figure A.1: PANES timing
.5
.4
.3
.2
.1
0
0
.1
.2
.3
.4
.5
.6
B. Baseline survey
.6
A. Application
2005m1
2005m7
2006m1
2006m7
2007m1
2007m7
2005m1
2005m7
2006m1
Date
2006m7
2007m1
2007m7
Date
D. First food card payment
0
0
.1
.1
.2
.2
.3
.3
.4
.4
.5
.5
.6
.6
C. First cash payment
2005m1
2005m7
2006m1
2006m7
2007m1
2007m7
2005m1
2005m7
2006m1
Date
2006m7
2007m1
2007m7
Date
.5
.4
.3
.2
.1
0
0
.1
.2
.3
.4
.5
.6
F. First cash transfer-Baseline survey
.6
E. Baseline survey-Application
0
5
10
15
20
25
0
Months
5
10
15
Months
i
20
25
30
Table A.1: Description of school outcomes
School outcome
Description
Reported school attendance
Whether child is attending school
Total absences
Unjustified absences+0.5*Justified absences (max. 20 a year)
Unjustified absences
Maximum 20 a year (with zero justified absences)
Justified absences
Maximum 40 a year (with zero unjustified absences)
Repetition
Whether student repeats or not regardless of the cause
Repetition due to absence
Repetition due to poor attendance
Repetition due to performance
Repetition due to insufficient learning
Promotion
Whether the student is promoted to next grade
Average score per school year
GPA
Qualifications are graded from 1 to 12
Minimum score to be promoted is 6
ii
Table A.2: Pre-program descriptive statistics on school outcomes by gender. 2004
School
Total
outcomes
Non - applicants
PANES applicants
Dif. Successful
Successful
Unsuccessful
- Unsuccessful
Girls
Total absences
Unjustified absences
30.315
38.406
33.010
27.121
5.889***
[37.178]
[47.140]
[39.679]
[33.682]
[0.688]
27.199
36.531
29.951
23.932
6.019***
[37.084]
[47.213]
[39.608]
[33.540]
[0.686]
6.338
4.031
6.232
6.476
-0.244
[9.103]
[6.902]
[9.288]
[8.892]
[0.169]
33.988
37.500
36.742
30.754
5.989***
[0.474]
[0.492]
[0.482]
[0.462]
[0.009]
16.008
18.750
17.735
13.976
3.760***
[0.367]
[0.397]
[0.382]
[0.347]
[0.007]
17.981
18.750
19.007
16.778
2.229***
[0.384]
[0.397]
[0.392]
[0.374]
[0.007]
64.022
59.375
60.983
67.595
-6.612***
[0.480]
[0.499]
[0.488]
[0.468]
[0.009]
7.292
7.737
7.254
7.329
-0.075**
[1.391]
[1.851]
[1.359]
[1.421]
[0.032]
Justified absences
Repetition
Rep. due to attendance
Rep. due to performance
Promotion
GPA
Boys
Total absences
Unjustified absences
35.687
29.788
38.846
32.472
6.374***
[40.487]
[45.721]
[42.600]
[37.873]
[0.874]
32.938
27.182
36.091
29.728
6.364***
[40.605]
[43.599]
[42.760]
[37.964]
[0.877]
5.616
5.545
5.641
5.590
0.050
[8.246]
[8.924]
[8.103]
[8.389]
[0.179]
44.072
33.333
46.584
41.563
5.020***
[0.497]
[0.479]
[0.499]
[0.493]
[0.011]
20.453
18.182
22.899
17.946
4.954***
[0.403]
[0.392]
[0.420]
[0.384]
[0.009]
23.619
15.152
23.684
23.618
0.066
[0.425]
[0.364]
[0.425]
[0.425]
[0.009]
53.802
63.636
51.016
56.602
-5.586***
[0.499]
[0.489]
[0.500]
[0.496]
[0.011]
7.030
7.095
7.035
7.026
0.009
[1.282]
[1.136]
[1.285]
[1.280]
[0.038]
Justified absences
Repetition
Rep. due to attendance
Rep. due to performance
Promotion
GPA
Standard deviations between brackets.
iii
Table A.3: Pre-program child and household characteristics
Child and household
characteristics
Gender (male =1)
Gender of household head
Age of household head
Unsuccessful
- Unsuccessful
43.557
42.595
44.804
-2.209***
[0.496]
[0.495]
[0.497]
[0.007]
35.923
33.326
39.292
-5.966***
[0.480]
[0.471]
[0.488]
[0.006]
41.129
39.882
42.746
-2.864***
[10.120]
[9.150]
[11.046]
[0.132]
6.828
6.592
7.133
-0.541***
[2.333]
[2.232]
[2.423]
[0.031]
773.198
568.934
1038.079
-469.145***
[493.900]
[296.478]
[567.477]
[5.741]
5.181
5.576
4.669
0.907***
[1.974]
[1.969]
[1.860]
[0.025]
0.567
0.703
0.391
0.312***
[0.793]
[0.851]
[0.671]
[0.010]
1.162
1.353
0.915
0.438***
[1.022]
[1.057]
[0.918]
[0.013]
1.415
1.546
1.245
0.301***
[0.944]
[0.985]
[0.858]
[0.012]
23427
13227
10200
Household size
Children below 5
Children aged 6 to 11
Children aged 12 to 17
Observations
Dif. Successful
Successful
Education of household head
Household income per capita
PANES applicants
Total
Standard deviations between brackets.
0
.2
.4
.6
.8
1
Figure A.2: PANES treatment and eligibility. Follow-up surveys
−.02
−.01
0
.01
.02
Predicted poverty
Note: A linear regression on each side of the threshold is fit to the data.
iv
Table A.4: Optimal order of polynomial for reported
school attendance. Follow-up surveys
Order
First follow-up survey
Second follow-up survey
1
834.372*
474.973
2
835.669
470.819
3
838.801
470.785*
4
842.496
474.216
5
842.496
474.216
Note: AIC refers to Akaike information criterion.
*Minimum AIC.
Table A.5: Program e↵ect in reported school attendance.
Follow-up surveys. Additional controls
(1)
(2)
(3)
(4)
0.125
0.196
0.128
0.196
[0.082]
[0.122]
[0.082]
[0.122]
687
687
687
687
0.052
-0.066
0.063
-0.051
[0.055]
[0.087]
[0.056]
[0.088]
Observations
655
655
655
655
Child controls
Yes
Yes
Yes
Yes
Household controls
Yes
Yes
Yes
Yes
Regional controls
No
No
Yes
Yes
First follow-up survey
Observations
Second follow-up survey
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: Odd columns include polynomial of degree 1 and even columns include
polynomial of degree 2. Columns (1) and (2) include same control as columns (5)
and (6) of Table 3 and add indicators for occupation status of household head
and for house materials of roof and floor. Column (3) and (4) additionally include
indicators for administrative regions.
v
Table A.6: Program e↵ect in reported school attendance. Second follow-up
survey. Polynomial terms of degree 3
(1)
(2)
(3)
(4)
(5)
(6)
(7)
0.080
0.127
0.062
0.090
0.062
0.064
0.090
[0.127]
[0.115]
[0.118]
[0.121]
[0.118]
[0.123]
[0.127]
Observations
691
691
671
671
671
655
655
Child controls
No
Yes
Yes
Yes
Yes
Yes
Yes
Household controls
No
No
Yes
Yes
Yes
Yes
Yes
Regional controls
No
No
No
Yes
No
No
Yes
Eligibility
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: Columns (2) to (4) include controls for children, household and regional characteristics as in Table 3.
Columns (5) to (7) include additional controls as in Table A.5.
Figure A.3: Program e↵ect on reported school attendance. Follow-up surveys
.5
.2
.6
.4
.7
.6
.8
.8
.9
1
B. Second follow-up survey.
1
A. First follow-up survey.
−.02
−.01
0
.01
.02
−.02
−.01
Predicted poverty
0
.01
.02
Predicted poverty
Table A.7: Optimal bandwidth for school outcomes. Secondary school records
Outcomes
Bandwidth
Total absences
8.9%
Unjustified absences
7.3%
Justified absences
7.6%
Repetition
10.5%
Rep. due to absence
9.0%
Rep. due to performance
9.7%
Promotion
12.2%
GPA
7.8%
vi
Table A.8: Optimal order of polynomial for school outcomes. Bandwidth 10 %.
Secondary school records
Outcomes
Order of polynomial
1
2
3
4
5
Total absences
134927.90*
134928.60
134930.90
134933.40
134935.70
Unjustified absences
134918.00*
134919.50
134921.10
134923.70
134926.20
Justified absences
97241.34*
97242.83
97241.95
97245.86
97249.52
Repetition
18340.66
18337.65
18340.36
18337.53*
18338.95
Rep. due to absence
13674.42*
13676.89
13679.43
13681.97
13685.02
Rep. due to performance
11270.13
11268.52*
11272.46
11272.07
11274.65
Promotion
18609.24
18606.90*
18609.63
18608.36
18609.90
GPA
28287.95
28287.09*
28290.74
28293.61
28294.52
Note: AIC refers to Akaike information criterion.
*Minimum AIC
vii
Figure A.4: Program e↵ect on school outcomes. 2007
B. Unjustified absences
20
25
25
30
30
35
35
40
40
45
A. Total absences
−.1
−.05
0
.05
.1
−.1
−.05
Predicted poverty
0
.05
.1
.05
.1
Predicted poverty
D. Repetition
4
.25
.3
5
.35
6
.4
7
.45
.5
8
C. Justified absences
−.1
−.05
0
.05
.1
−.1
−.05
Predicted poverty
0
Predicted poverty
G. Rep. due to performance
.1
.1
.15
.15
.2
.25
.2
.3
.25
.35
F. Rep. due to attendance
−.1
−.05
0
.05
.1
−.1
Predicted poverty
−.05
0
Predicted poverty
viii
.05
.1
Table A.9: Program e↵ect in school outcomes. Bandwidth 10%.
Additional controls. 2007
Total absences
Unjustified absences
Justified absences
(1)
(2)
(3)
(4)
-2.718⇤
-4.903⇤⇤
-2.651
-4.412⇤
[1.637]
[2.416]
[1.624]
[2.411]
-2.731⇤
-4.816⇤⇤
-2.714⇤
-4.416⇤
[1.636]
[2.415]
[1.622]
[2.409]
-0.110
-0.213
-0.051
-0.003
[0.419]
[0.631]
[0.416]
[0.623]
-0.039⇤
-0.045
-0.036⇤
-0.042
[0.020]
[0.030]
[0.020]
[0.030]
-0.040⇤⇤
-0.030
-0.037⇤⇤
-0.024
[0.017]
[0.026]
[0.017]
[0.026]
0.001
-0.015
0.001
-0.017
[0.016]
[0.024]
[0.016]
[0.024]
0.037⇤
0.049
0.035⇤
0.046
[0.020]
[0.031]
[0.020]
[0.031]
0.031
0.118
0.050
0.139
[0.075]
[0.114]
[0.076]
[0.115]
Observations
12836
12836
12836
12836
Observations (GPA)
7841
7841
7841
7841
Child controls
Yes
Yes
Yes
Yes
Household controls
Yes
Yes
Yes
Yes
Regional controls
No
No
Yes
Yes
Repetition
Rep. due to attendance
Rep. due to performance
Promotion
GPA
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Note: odd columns include polynomial of degree 1 and even columns include polynomial
of degree 2. Columns (1) and (2) include same control as columns (7) and (8) of Table
4 and add indicators for occupation status of household head and for house materials
of roof and floor. Column (3) and (4) replace indicators of administrative regions for a
more disaggregated regional variable (localidades).
ix
Table A.10: Optimal order of polynomial for school outcomes. Bandwidth 6, 15
and 20 %. Secondary school records
Outcomes
Order of polynomial
1
2
3
4
5
Bandwidth 6 %
Total absences
85457.64*
85461.50
85464.82
85466.50
85469.83
Unjustified absences
85418.88*
85422.60
85426.13
85427.37
85430.28
Repetition
11544.97*
11548.96
11547.02
11550.89
11554.23
Rep. due to absence
8539.33*
8543.20
8547.02
8549.73
8552.51
Bandwidth 15 %
Total absences
164430.60
164414.50*
164417.60
164416.80
164419.70
Unjustified absences
164454.80
164440.00*
164443.30
164441.80
164444.80
Repetition
22491.95
22477.24
22476.83
22472.92
22468.06*
Rep. due to absence
16946.47
16942.40*
16944.07
16943.92
16945.84
Bandwidth 20 %
Total absences
192277.70
192273.00
192267.20*
192269.70
192267.40
Unjustified absences
192336.40
192332.70*
192328.30
192330.20
192327.30
Repetition
26387.72
26387.03
26373.03*
26373.86
26374.25
Rep. due to absence
20069.79
20067.12*
20068.04
20067.94
20068.91
Note: AIC refers to Akaike information criterion.
*Minimum AIC
x
Table A.11: Program e↵ect in school outcomes. Bandwidth
6%. 2007
(1)
(2)
(3)
(4)
-3.832⇤
-4.102⇤⇤
-3.979⇤
-3.510⇤
[2.146]
[2.057]
[2.042]
[2.034]
-3.778⇤
-4.055⇤⇤
-3.864⇤
-3.401⇤
[2.136]
[2.052]
[2.037]
[2.029]
-0.212
-0.199
-0.323
-0.317
[0.532]
[0.527]
[0.533]
[0.534]
-0.029
-0.032
-0.028
-0.025
[0.027]
[0.026]
[0.026]
[0.026]
-0.026
-0.029
-0.029
-0.024
[0.023]
[0.022]
[0.022]
[0.022]
-0.003
-0.003
0.001
-0.001
[0.021]
[0.020]
[0.020]
[0.020]
0.018
0.035
0.031
0.042
[0.098]
[0.097]
[0.097]
[0.096]
Observations
8388
8388
8199
8199
Observations (GPA)
5193
5193
5085
5085
Total absences
Unjustified absences
Justified absences
Repetition
Rep. due to absence
Rep. due to performance
GPA
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
All columns include polynomial expressions on the score of grade 1. Column (2)
includes child characteristics, column (3) includes household characteristics and column
(4) additionally inlcude indicators for five administrative regions, month of enrollment
and month of baseline survey as in Table 4.
xi
Table A.12: Program e↵ect in school outcomes. Bandwidth 15%. 2007
(1)
(2)
(3)
(4)
-5.544⇤⇤⇤
-5.884⇤⇤⇤
-5.678⇤⇤⇤
-4.441⇤⇤
[2.139]
[2.077]
[2.062]
[2.062]
-5.690⇤⇤⇤
-6.019⇤⇤⇤
-5.749⇤⇤⇤
-4.476⇤⇤
[2.132]
[2.071]
[2.056]
[2.058]
0.039
0.020
-0.085
-0.132
[0.522]
[0.519]
[0.525]
[0.523]
-0.054⇤⇤
-0.057⇤⇤
-0.052⇤⇤
-0.043⇤
[0.027]
[0.026]
[0.026]
[0.026]
-0.051⇤⇤
-0.053⇤⇤
-0.051⇤⇤
-0.043⇤
[0.022]
[0.022]
[0.022]
[0.022]
-0.002
-0.004
-0.002
-0.001
[0.021]
[0.020]
[0.021]
[0.020]
0.049⇤
0.053⇤⇤
0.049⇤
0.040
[0.027]
[0.026]
[0.026]
[0.026]
0.052
0.065
0.065
0.059
[0.096]
[0.095]
[0.096]
[0.094]
Observations
16124
16123
15757
15757
Observations (GPA)
9696
9696
9492
9492
Total absences
Unjustified absences
Justified absences
Repetition
Repetition due to attendance
Repetition due to performance
Promotion
GPA
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
All columns include polynomial terms of order 2 Column (2) includes child characteristics, column
(3) includes household characteristics and column (4) additionally inlcude indicators for five administrative regions, month of enrollment and month of baseline survey as in Table 4.
xii
Table A.13: Program e↵ect in school outcomes. Bandwidth 20%. 2007
Total absence
Unjustified absences
Justified absences
Repetition
Rep. due to absence
Rep. due to performance
Promotion
GPA
Observations
Observations (GPA)
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
-2.277
[1.877]
-2.464
[1.871]
0.193
[0.462]
-0.017
[0.023]
-0.033⇤
[0.020]
0.016
[0.018]
0.014
[0.024]
0.008
[0.086]
-7.120⇤⇤⇤
[2.501]
-7.034⇤⇤⇤
[2.493]
-0.306
[0.622]
-0.082⇤⇤⇤
[0.031]
-0.060⇤⇤
[0.027]
-0.022
[0.024]
0.077⇤⇤
[0.032]
0.117
[0.115]
-2.762
[1.799]
-2.932
[1.798]
0.165
[0.458]
-0.022
[0.022]
-0.036⇤
[0.019]
0.014
[0.018]
0.019
[0.023]
0.022
[0.084]
-7.419⇤⇤⇤
[2.388]
-7.335⇤⇤⇤
[2.387]
-0.298
[0.615]
-0.085⇤⇤⇤
[0.030]
-0.063⇤⇤
[0.026]
-0.023
[0.024]
0.083⇤⇤⇤
[0.030]
0.147
[0.114]
-2.831
[1.807]
-2.921
[1.805]
0.031
[0.466]
-0.024
[0.023]
-0.038⇤⇤
[0.019]
0.014
[0.018]
0.021
[0.023]
0.029
[0.085]
-7.280⇤⇤⇤
[2.361]
-7.127⇤⇤⇤
[2.359]
-0.421
[0.621]
-0.079⇤⇤⇤
[0.030]
-0.059⇤⇤
[0.026]
-0.019
[0.024]
0.078⇤⇤⇤
[0.030]
0.151
[0.114]
-2.709
[1.804]
-2.712
[1.805]
-0.117
[0.462]
-0.034
[0.022]
-0.037⇤
[0.019]
0.003
[0.018]
0.032
[0.023]
0.062
[0.084]
-5.632⇤⇤
[2.363]
-5.501⇤⇤
[2.363]
-0.367
[0.619]
-0.060⇤⇤
[0.030]
-0.049⇤
[0.026]
-0.011
[0.024]
0.058⇤
[0.030]
0.114
[0.112]
18830
11187
18830
11187
18830
11187
18830
11187
18407
10953
18407
10953
18407
10953
18407
10953
Robust standard errors clustered by score.
⇤ , ⇤⇤ , ⇤⇤⇤ significant at 90, 95 and 99% levels respectively.
Odd columns include polynomial expressions on the score of grade 2 and even of order 3. Column (3) and (4) include
child characteristics, column (5) and (6) includes household characteristics and columns (7) and (8) additionally inlcude
indicators for five administrative regions, month of enrollment and month of baseline survey as in Table 4.
xiii
Figure A.5: Program e↵ect on school outcomes. Girls. 2007
20
20
30
30
40
40
50
50
60
B. Unjustified absences
60
A. Total absences
−.1
−.05
0
.05
.1
−.1
−.05
Predicted poverty
0
.05
.1
.05
.1
Predicted poverty
D. Repetition
4
.2
5
.3
6
.4
7
.5
8
.6
9
.7
C. Justified absences
−.1
−.05
0
.05
.1
−.1
−.05
Predicted poverty
0
Predicted poverty
0
.1
.1
.2
.2
.3
.3
.4
G. Rep. due to performance
.4
F. Rep. due to attendance
−.1
−.05
0
.05
.1
−.1
Predicted poverty
−.05
0
Predicted poverty
xiv
.05
.1