Compensation vs. Reinforcement: Experimental
Identification of Parental Aversion to Inequality
in Offspring
Felipe Barrera-Osorio, Leonardo Bonilla, Matias Busso, Sebastian Galiani,
Hyunjae Kang, Juan Muñoz-Morales, Juan Pantano*
June 12, 2023

Abstract
The allocation of resources within the household has been extensively theorized,
but empirical evidence on this topic has been very scarce. Endogeneity concerns
hinder this type of analysis due to the lack of identifying variation within thehousehold. In this paper, we overcome these difficulties by exploiting a uniquesetting that introduced random variation in resource allocation within households.
We evaluate the effects of a program that provided alternative delivery methods of conditional cash transfers in Bogotá, Colombia, and allocated resources atthe student level. The individual randomization implied that some households
had treated and untreated siblings, allowing us to extend the analysis to estimate
spillover effects of the program on beneficiaries and their siblings. Students wererandomly allocated to a standard design and a design that prioritized enrollment
in tertiary education. We find that standard delivery methods increase educational outcomes for treated children but decrease the same outcomes for untreatedsiblings of treated students. We rationalize the results by estimating a structuralmodel that uses the standard delivery method for estimation and the alternative
delivery method for validation

Keywords: Spillover effects, conditional cash transfers, intra-household, Colombia.
JEL codes:* Barrera-Osorio: Vanderbilt University (felipe.barrera.-.osorio@vanderbilt.edu); Bonilla: Banco dela República (lbonilme@banrep.gov.co); Busso: Inter-American Development Bank (mbusso@iadb.org);
Galiani: University of Maryland (sgaliani@umd.edu); Kang: Kyoto University (kang.hyunjae@stonybrook.edu ); Muñoz-Morales: IESEG School of Management, Univ. Lille, CNRS, UMR 9221LEM-Lille Économie Management, F-59000 Lille, France (j.munoz@ieseg.fr); Pantano: University of Arizona (jpanta@arizona.edu). We thank Julian Martínez-Correa for great research assistance. For helpful
discussion and comments, we thank seminar participants at LACEA. The opinions expressed in thisdocument are those of the authors and do not necessarily reflect the views of the Inter-American Development Bank, its Board of Directors, and the countries they represent. Errors are our own.

1

Introduction

Household theory treats the household as a unit, and different models treat allocation of resources and tasks in different ways. In Becker’s canonical model, parents
allocate resources among children based on initial endowment of skills (Becker andLewis, 1973). Several lines of research, including bargaining power strategy, have expanded this theoretical frontier to include decisions within households as determinants of economic behavior (Chiappori, 1988). While this theoretical literature has
been extensively developed, empirical contributions have been more limited in theirability to adequately test some of the model’s predictions.
Empirical estimations of household decisions are remarkably challenging to perform due to numerous potential sources of bias. Resource allocation among household
members is based on unobserved characteristics, which hinder the existence of exogenous variation in resources and incentives. This paper contributes to addressing thisproblem by analyzing a unique setting that randomly assigned cash transfers within
the household.
In 2005, local authorities in Bogotá, Colombia, implemented an evaluation of alternative delivery methods of conditional cash transfer programs aimed at reducing
dropout rates in secondary education among low-income students. The intervention
was implemented in two out of the 12 localities of Bogotá, under the Conditional Subsidies for School Attendance Program ("Subsidios Condicionados a la Asistencia Escolar", in Spanish). Participating students were randomized into two different treatments. The first treatment followed standard delivery methods and provided monthly
stipends summing up to a fixed annual rate of 300,000 Colombian pesos (approximately $150 USD) (referred to as the “Basic” treatment hereafter). The second treatment varied the timing of the transfer. It provided two-thirds of the standard amount(i.e., 20,000 COP, monthly), but upon high school graduation, students received an additional amount of 600,000 COP ($300 USD) immediately if they enrolled in a tertiary
education program or one year after if they did not enroll (referred to as the “College”
treatment hereafter).
The program randomly assigned treatment at the student level, making this a very
unique setting. In households with multiple participants, all children could be treated,
untreated, or some treated. This allocation method differs from previous studies because it introduces within-household variation in treatment status, randomly varying
the allocation of resources within the household. This approach allows us to estimate
spillover effects of transfers within households and empirically test the implicationsof the canonical models of household resource allocation.
We exploit this unique setting to estimate the direct and indirect effects of conditional cash transfers on resource allocation within the household. We compare therandomly assigned treated groups to estimate the direct effects of the basic and college
treatments. To estimate the indirect effects of the treatments, we compare untreated individuals whose siblings were treated with untreated individuals in households whereanyone was treated. We restrict this comparison to households with only two children
since larger households have a higher likelihood of having treated siblings.
1

We combine a comprehensive set of data from various sources to estimate shortand long run outcomes. In the short run, we analyze data collected within a year after
the intervention to measure school attendance, school enrollment, and working status.
In the long run, we link administrative data sets to identify high school graduation,college enrollment, and college graduation.
The basic treatment had short run direct effects that disappear over time. More
importantly, we find that this treatment reduced school attendance and enrollment of
untreated siblings, leading to a substantial long-term decrease in college enrollment
and graduation. These effects are sizable implying a 12 and 30 percent decrease incollege enrollment and graduation rates, respectively, compared to the control mean.
In contrast, the college treatment increased attendance and enrollment of treatedchildren but had no spillover effects on untreated siblings. Treated students showed
increased school attendance, enrollment, and a reduced likelihood of working duringhigh school. These effects resulted in a notable long-term increase of 12 percent in college enrollment compared to the control mean. Nonetheless, we do not observe any
spillover effects of the college treatment among untreated siblings.
Our findings suggest that when resources are randomly allocated, parents reinforce
the resources of their offspring by prioritizing short-term educational investments. To
explain these results and explore the key mechanisms driving our findings, we develop a dynamic structural model. This model allows households to make decisions
about which children attend school, their level of school attendance, and which ofthem work. The model considers decisions made by households for each child fromlate childhood through the teenage years and into early adulthood.
Following Galiani, Murphy, and Pantano (2015) and Galiani and Pantano (2022),
we estimate the model by exploiting only a portion of the randomized variation available in the experiment. The remaining portion is reserved for model validation, following the approach of Todd and Wolpin (2006). Specifically, we employ a simulationbased estimation approach that seeks to identify the structural parameters that best
replicate the effects of the Basic treatment (both short-run and long-run, direct andindirect) as observed in the experiment. We then validate the model’s performanceout of sample by assessing its ability to reproduce the distinct set of estimated effects
found for the College treatment.
The conditional cash transfer experiment at the student level introduces fully exogenous, randomized variation across siblings in the opportunity costs of sending
them to school. This variation provides a unique opportunity to convincingly identify the extent of parental aversion to inequality in educational outcomes among theiroffspring, a parameter introduced by Behrman, Pollak, and Taubman (1982) in the literature on parental investment in children.
Once the model is estimated and validated, we use it to understand the mechanisms underlying the observed negative spillovers on untreated children who havea sibling treated with either the Basic or College treatment. Additionally, we use the2model to inform the optimal design of conditional cash transfers, taking into accountspillovers across siblings.
The rest of the paper is organized as follow. The next section summarizes the relevant literature and places our contributions in the context of that literature. Section
3 describes the experimental intervention and Section 4 describes our approach to estimate the treatment effects from the experiment. Section 5 provides details on theextensive sets of data sources that we use. Section 6 previews the main reduced form
findings from the experiment that we later use to estimate and validate the structuralmodel. Section 7 fleshes out the structural model in detail and Section 8 provides
details of our simulation-based, structural estimation strategy.

2

Related Literature and Contribution

This paper builds on work performed by Barrera-Osorio et al. (2011) and BarreraOsorio et al. (2019), who estimate the short and long run effects, respectively, of theConditional Subsidies for School Attendance Program. These papers mainly focus on estimating the direct effects of the program. We validate their results and extend theanalysis to include the estimation of spillover effects on siblings and the structuralmodeling of the transfers. The inclusion of the model contributes to the understandingof the underlying mechanisms behind the cash transfers and the dynamics of resource
reallocation within households.
In addition, our work contributes to four lines of literature. First, our results relate
to the broad body of work that examines the impacts of conditional cash transfers on
different margins. Since the initial evaluations of Progresa in Mexico, multiple studies have assessed the short-run effects of conditional cash transfers on a wide rangeof outcomes. These studies generally show that conditional cash transfers increase
school enrollment across different settings. For example, Behrman, Sengupta, andTodd (2005), Todd and Wolpin (2006), and Attanasio, Meghir, and Santiago (2012) analyze the short-term effects of Progresa and consistently find positive effects on school
attainment using reduced form and structural methods. Moreover, Attanasio, Fitzsimons, Gomez, Gutiérrez, Meghir, and Mesnard (2010) evaluates a conditional cashtransfer program in Colombia (i.e., familias en acción) and again finds increases inschool enrollment.
By contrast, evidence on the long-run effects of conditional cash transfers is relatively limited in the literature. The available evidence suggests that conditional cashtransfers have positive effects on schooling but limited effects on longer-term outcomes such as cognitive skills, learning, socio-emotional skills, employment, and earnings (Barham, Macours, and Maluccio, 2017; Barrera-Osorio, Linden, and Saavedra,
2019; Cahyadi, Hanna, Olken, Prima, Satriawan, and Syamsulhakim, 2020; Molina
Millán, Macours, Maluccio, and Tejerina, 2020). Many of these results face methodological challenges and are not fully capable to determine whether the insignificant
point estimates reflect a lack of effect or methodological difficulties (Millán, Barham,
Macours, Maluccio, and Stampini, 2019).

3

To the best of our knowledge, our work is the first in the literature on conditional
cash transfers to estimate spillover effects within the household. Previous studies typically analyze interventions where transfers are allocated at the household level, whichhinders the estimation of within-household spillovers. Our work suggests that conditional cash transfers have the power to alter resources and behavior within the household when they are assigned at the student level.
Second, our work contributes to the literature on spillover effects of policy interventions (see Angelucci and Maro (2016) for a review). In a seminal paper, Miguel andKremer (2004) measure the spillover effects of deworming on health and school participation. Additionally, some studies specifically focus on spillover effects across treatedand untreated households in conditional cash transfer programs. For instance, Angelucci and De Giorgi (2009) and Bobonis and Finan (2009) identify positive spillover
effects of cash transfers on ineligible households and neighborhood peers. We contribute to this literature by exploiting random variation to identify within-household
spillover effects. These effects analyze different margins that complement those on
ineligible households and neighborhood peers.
Third, we contribute to a line of research that emphasizes the value of combining
randomized control trials with structural modeling (Todd and Wolpin, 2020). A small
but growing literature integrates dynamic structural models and randomized control
trials to evaluate conditional cash transfer programs (Todd and Wolpin, 2006; Attanasio, Meghir, and Santiago, 2012; Galiani, Pantano, and Shi, 2022). More generally, we
contribute to a stream of this literature, as discussed in Galiani and Pantano (2022),
that emphasizes the dual role of multi-arm randomized control trials, which can beused to both estimate and validate structural models (e.g., Galiani et al. (2015), andGaliani et al. (2022)).
Fourth, and more substantively, our work contributes to the literature that explores the question of whether parents tend to compensate or reinforce differencesamong siblings. In a seminal paper, Becker and Tomes (1976) first proposed this question by relaxing the assumption of equal endowments in earlier work by Becker andLewis (1973) on the quantity-quality trade-off. In a highly influential follow-up to
this paper, Behrman, Pollak, and Taubman (1982) introduced parental aversion to inequality in offspring outcomes and used a sample of twins to estimate a static, singleshot structural model, concluding that parents display substantial aversion to inequality in offspring and this leads them to compensate for differences in initial endowments. Rosenzweig and Wolpin (1988) introduced sequential decision-making anduncertainty into this literature, noting that the single-shot model is simple but quite
unrealistic, as the parental investment process is dynamic and sequential. More recently, Aizer and Cunha (2012) exploit exogenous variation from the initial launch of
Head Start in 1966 and show that parents, through their investments, tend to reinforce
initial endowment differences across siblings. In a recent relevant paper, Carneiro,
Rasul, and Salvati (2023) study a prenatal intervention that provides information andcash transfers to parents based on a verified pregnancy of a target child. Their results
suggest that parents reinforce inputs across siblings in the first 1000 days of life window.

4

Our work adds to the literature on compensation vs. reinforcement of differencesamong siblings by exploiting a unique setting that introduced random variation acrosssiblings within the household and by observing long-term effects up to graduationfrom college. Furthermore, we formulate and estimate a dynamic structural modelthat rationalizes the decisions a household makes about each of the siblings and theresulting spillover effects. The substance of this model is inspired by the foundational
work of Behrman, Pollak, and Taubman (1982), but its implementation mechanics relyon the more modern formulation of estimable dynamic structural models, as in Todd
and Wolpin (2006). Moreover, the experimental variation from the conditional cashtransfer intervention provides a key source of identification for the parental inequality
aversion parameter. Furthermore, a held-out group of households where a lotterywinning sibling was treated with an alternative cash transfer design is used for out-ofsample validation to enhance the credibility of the model. The estimated model allows
us to understand the underlying mechanisms that generate spillovers across siblings
and helps us think about the optimal conditional cash transfer design in the context of
those spillovers.

3

Experimental Intervention

Dropout rates in secondary education were high at the beginning of the 2000s in
Latin America (Bassi, Busso, and Muñoz, 2015). Many countries, including Colombia,
adopted strong policies targeted at decreasing school dropout rates. Conditional cashtransfers had proven to be a successful policy after showing promising results acrossthe region (Behrman, Sengupta, and Todd, 2005; Todd and Wolpin, 2006; Attanasio,
Fitzsimons, Gomez, Gutiérrez, Meghir, and Mesnard, 2010; Attanasio, Meghir, andSantiago, 2012).
Therefore, in an effort to address high dropout rates in secondary education, publicauthorities in Bogotá, Colombia, carried out in 2005 the evaluation of the conditional
Subsidies for School Attendance Program. The intervention tested alternative delivery
methods of conditional cash transfers. It was implemented in two out of the 12 localities of Bogotá, and targeted exclusively low-income households whose children wereenrolled in secondary education.

3.1

Timeline of Intervention

The experiment began in 2004, during which baseline data was collected prior to
the intervention. The information was gathered using the "System of Identificationof Social Program Beneficiaries" (SISBEN), which collects data on low-income households and categorizes them to target social spending.1
Two localities in Bogotá with a high prevalence of low-income households, San
Cristóbal and Suba, were selected as the sites to conduct the experiment. A robust
1 This system is originally named "Sistema de Identificación de Potenciales Beneficiarios de Pro-

gramas Sociales" in Spanish, and it collects information about households that may be classified as
low income. This information is used to calculate a poverty index designed to target social programs
throughout the country.

5

advertising campaign was conducted in these two areas during January and earlyFebruary of 2005. The program was promoted as one that offered incentives for schoolparticipation. Subsequently, in late February and March, a 15-day registration period
was opened, allowing parents to enroll their children as potential candidates for the
program.
To be eligible for the program, several criteria had to be met: 1) at least one parent
had to be present during the registration process; 2) students had to have completed
fifth grade; 3) students had to be enrolled in secondary education but not have graduated yet; and 4) the family needed to be classified within the two lowest categories of
the SISBEN index. A total of 17,225 students (from 12,674 households) registered andmet the criteria, with 63 percent from San Cristóbal and 36 percent from Suba.2 The
city allocated sufficient funds to provide subsidies to 56 percent of the students, with
39 percent of them in San Cristóbal and 17 percent in Suba.
Parents were not obligated to register all of their children in the household, resulting in some children being excluded from the experiment, even though their siblings
could have been registered. Regarding the distribution of households, 70 percent (ofthe 12,674 households) registered only one individual, while 25 percent registered two
individuals. Additionally, 5 percent of households registered three individuals, andthe remaining 1 percent of households registered four or five individuals.
The assignment of treatment was carried out publicly and randomly on April 4,
2005, with strict surveillance, and the lists of beneficiaries were immediately printed.
The randomization process was stratified based on site, type of school, grade, and gender.
Importantly, the randomization was performed at the student level, which meansthat some children within the same household were assigned to the treatment group,
while others were not. This randomization created variation in treatment status withinhouseholds, allowing for a comparison between treated and untreated individuals.
Later, between May and July 2005, baseline data on the participants was collected
through a student-level survey. The survey was designed as a self-administered questionnaire that students completed during their classes. However, due to budget limitations, the survey and subsequent attendance data collection were carried out only inthe 68 schools with the highest number of registered children. This subset of schools
accounted for a total potential sample of 9,715 students, which represented 56 percentof the overall registered students.
The transfers under the program commenced in July 2005, which was during the
middle of the school year. It is worth noting that the academic year for public schoolsin Colombia typically starts in January and concludes in November. Data collection
on students’ attendance took place between October and December 2005, utilizing direct observation methods. In February and March 2006, a follow-up survey was conducted. This survey was administered at the household level to ensure that students
who had dropped out of school were accounted for. Remarkably, almost all of the
2 We drop 84 because they were out of school before the program started.

6

individuals from the baseline (8,736 out of 8,896, or 98.14 percent) were successfully
located and included in the follow-up survey.

3.2

Treatment Arms

The program aimed to evaluate various delivery methods of conditional cash transfers by randomly assigning students to two different treatment arms (Barrera-Osorio
et al., 2011, 2019):
1. The “Basic” conditional cash transfer provided participant families with 300,000
Colombian pesos (approximately $150 USD) yearly if the student attended 80
percent of the classes. The money was distributed every two months, with beneficiary families receiving 60,000 pesos (30,000 pesos per month) in each installment.3
2. The “College” treatment involved varying the timing of the transfer. Under
this treatment, students received two-thirds of the original bi-monthly amount(20,000 COP, monthly), but upon high school graduation, they received a totalsum of 600,000 COP ($300 USD). The amount was granted immediately if thestudent enrolled in a tertiary education program, or after one year if the student
did not enroll.
The transfer amount in the college treatment was larger than in the basic treatment,
and the delivery method prioritized tertiary education enrollment. It is important tonote that participating families were not aware of the existence of multiple treatment
options at the time of registration.
Randomization by Sites. The implementation of treatment assignment differed between the two localities. In San Cristóbal, eligible participants ranging from 6th to11th grades were randomly assigned to the control group or the basic treatment. On
the other hand, in Suba, students in 6th to 8th grades were randomized into the control group or the basic treatment, while students in 9th to 11th grades were randomly
assigned to either the control group or the college treatment.4

4

Experimental Analysis of the Intervention

The treatment was randomly assigned at the student level, so families with eligible
children could have been fully treated, partially treated, or had received no treatment
at all. We exploit this variation to estimate direct and indirect effects of the college andbasic treatments.

3 Some of the households assigned to this treatment received two-thirds of the amount (20,000 COPor roughly $10 USD) every two months, while the remaining one-third was saved in a bank account andmade available at the beginning of the next academic year. Both delivery methods provided approximately the same amount of money, making them income-neutral. We pool together these two delivery
methods as they are equivalent for the sake of this project.
4 In our main specifications we include site and grade dummies to account for this heterogeneity.

7

4.1

Direct Effects

We estimate the direct effects on treated individuals by comparing outcomes of students that won the lottery and those who lost. These effects are computed at the shortand at the long run. The estimations using short-run outcomes correspond to thosepresented in Barrera-Osorio et al. (2011). The estimations using long term outcomescorrespond to those displayed in Barrera-Osorio et al. (2019).
To increase statistical power, we pool both sites into an aggregate estimation, but
separate by treatment arms. Formally, we estimate:DDD
Yi = β D
B,0 + β B Basici + β B,X Xi + ε i ,(1)for the basic treatment, and :DDD
Yi = β D
C,0 + β C Collegei + β C,X Xi + ε i ,(2)for the college treatment. Yi corresponds to a given outcome measured either in the
short or the long run. Xi corresponds to a vector that includes a site dummy, a dummythat takes the value of one if the student is in 9th grade or higher, and the interaction
between these two. We compute heteroskedasticity-consistent standard errors.5

4.2

Indirect Effects

We compute indirect treatment effects on outcomes of siblings of treated students.
Siblings are defined as those individuals living in the household that are descendants
either of the household head or the spouse (or both). To estimate these effects we compare control individuals in households with treated siblings with control individuals
in households where no one was treated. We restrict the estimations to householdswith only two registered children because this it the most reliable comparison. Including households with more registered students can be worrisome as a larger number ofregistered individuals increases the likelihood of receiving treatment.
To make things clear, assume three households, X, Y, and Z, each one with two registered students. By random assignment, one of these households, X, gets two treatedsiblings X1 = 1 and X2 = 1 (Xi corresponds to individual i in household X). The
second household randomly gets one treated individual and another one not, Y1 = 1,Y2 = 0, while the third gets not treatment at all, Z1 = 0, Z2 = 0. Our strategy estimatesthe indirect sibling effects by comparing Y2 with Z1 and Z2 . None of these students
was treated, but one, Y2 , had a sibling that did. Note that restricting to families with
only two siblings, and excluding directly treated students, automatically drops thosefamilies with two registered students where both students were treated with in any
way.
Formally, we estimate:
Yi = βSB,0 + βSB Sibling Basici + βSB,X Xi + εSi ,(3)

5 We implement Huber-White robust standard errors because the treatment varies at the individuallevel (Abadie et al., 2022). The results are, nonetheless, robust to alternative approaches like clustering
standard errors at the school level.

8for the basic treatment, andYi = βSC,0 + βSC Sibling Collegei + βSC,X Xi + εSi ,(4)

for the college treatment. Yi again correspond to short and long run outcomes. Sibling Collegei
and Sibling Basici are dummies that take the value of one if a member in the household was treated either with the college or with the basic treatment, respectively, andzero if none were treated. Xi includes a dummy for the site of the experiment, and wecompute heteroskedasticity-consistent standard errors.

5

Data

To track both short-term and long-term outcomes of the students in the experiment, we use a comprehensive set of data sources. Our data includes a universe ofhouseholds that were surveyed one year after the randomization, which corresponds
to nine months after the first transfer took place. Additionally, we compute long-term
outcomes by merging the universe of households with administrative data sourcesthat span up to 11 years after the intervention.6

5.1

Experimental Baseline Data

Our universe of analysis consists of the 17,225 students who were initially registered in the experiment. We identify these individuals using two primary data sources:• Registration Data: This dataset includes information on the students who registered for the program and resided in the two treated localities in Bogotá. During
the registration process, families provided basic information about the students.
• Lottery Data: These data provide information on the individual-level lottery conducted in San Cristóbal and Suba, stratified by different grade levels.
By combining the SISBEN data with the registration and lottery datasets, we are able
to accurately identify and analyze the individuals who participated in the experiment.

5.2

Short Run Data Sources

After the intervention, data on enrollment were collected through administrative
sources. Due to budget constraints, however, follow-up information on attendance
and other outcomes was only gathered for students registered in the 68 schools withthe highest number of registered students.
Enrollment Data: Information about school enrollment was gathered from administrative records of the city of Bogotá. Enrollment records include information about
students enrolled at the beginning of the school year. School calendars in Bogotá startin January, implying that information on school enrollment was collected about six
months after the intervention, at the beginning of the next academic year. Students
6 For more information about the specific details regarding the merging of these data sets, pleaserefer to Appendix D.

9

in the last grade (i.e., 11th grade) were not included as they were not eligible because
they had, very likely, already graduated. Not all students were successfully mergedwith the registration data because they could have either attended schools that did
not report attendance to the local authorities or there was simply not enough information for a successful merge. Nonetheless, enrollment status of more than 90 percent ofparticipating students was matched with the administrative records (Barrera-Osorio,
Bertrand, Linden, and Perez-Calle, 2011).
Attendance Data: The collection of attendance data took place during the last quarter of 2005. Only students in the 68 schools with the highest number of registeredstudents were selected to be surveyed. Enumerators visited schools and classrooms
randomly over a period of 13 weeks to record attendance information of the selectedstudents. These data provided insights into the students’ attendance patterns following the intervention.
Follow-up Survey: In March 2006, a follow-up survey was conducted to gather additional information of the participating students who were enrolled in the selected
68 schools. These students were interviewed in their households to ensure that those
who had dropped out of school after the intervention were still observed. The researchteam located the families of 98 percent of students. This implies that more than half
(56 percent) of the individuals who were originally registered in the experiment wereinterviewed during the follow-up survey in March 2006.7 .
Dropout among the three sub-samples measuring enrollment, attendance, and followup information was similar across the three different research groups. We can therefore rule out any selective attrition across treatment arms that could bias our research
design. More information about this can be found in Barrera-Osorio et al. (2011).

5.3

Long Run Data Sources

We employ the second wave of the administrative census for low-income households (i.e., SISBEN), which was gathered in 2004, to reconstruct families in the longterm. SISBEN serves as a valuable resource for identifying households and household
members. The SISBEN data is derived from a comprehensive census of low-income
households conducted nationwide. It contains detailed socio-demographic information about members of the household.
The experimental data, combined with the SISBEN data, include individual national identification numbers of program beneficiaries (students) and their family members. These identification numbers enable us to link the sample, as well as their household members, to various long-term administrative data sources. As a result, we cantrack the students and their family members from the time of the experiment up to 11
years after the intervention.
To compute long run outcomes, we incorporate two additional data sets from theColombian education system. Firstly, we merge the experimental records with test
7 For further details regarding the collection of follow-up data, additional information can be foundin the study by Barrera-Osorio, Bertrand, Linden, and Perez-Calle (2011)10

scores obtained from the high school exit exam called “Saber 11” between 1996 and2015. This exam evaluates all students who aim to obtain a high school diploma at thetime of their graduation. It covers multiple subjects, and the results are utilized forcollege admission purposes. Taking the exam is a requirement for graduation, making
it a very close proxy for high school completion. It is worth noting that over 90 percent
of test takers successfully graduate from high school after taking this exam.
Secondly, we assess college attendance by leveraging the administrative records ofstudents who enrolled in any tertiary education program. These records are obtained
from the “SPADIES” dataset, which includes data from 1998 to 2016. According to
Colombian law, all tertiary education institutions are obligated to report information
about their students to the Ministry of Education. The dataset includes details about
students’ majors, enrollment status, graduation, and dropout rates.
By integrating these data sources, we gained comprehensive insights into the educational trajectories of the students, including their performance in high school andtheir participation in tertiary education programs.

5.4

Outcomes

The analysis of the effects of the program includes two different sets of outcomes,
depending on the timing of measurement. First, we examine the short-term effects ofthe treatments on school enrollment, attendance, and working status. School enrollment is computed directly from the administrative records, whereas school attendanceis calculated using the information on schools visits in the 68 selected schools, andworking status is computed using data from the household follow-up surveys. These
short-run measures are constructed following the methodology outlined by BarreraOsorio, Bertrand, Linden, and Perez-Calle (2011).
Second, we investigate the long-term effects by merging the experimental sample
with the data from the high school exit exam and college enrollment records, as conducted in Barrera-Osorio, Linden, and Saavedra (2019). These administrative data setsencompass the entire population of individuals who took the high school exit exam orenrolled in tertiary education institutions. Consequently, the absence of a person fromthe experimental sample in the merged data constitutes an outcome in itself. By linking the experimental sample with these administrative data sets, we are able to construct measures of high school graduation, college enrollment, and college graduation.
We use the household follow-up survey and the second wave of SISBEN to identify siblings. In the short run, we fully identify siblings and their outcomes using thefollow-up surveys. These surveys were conducted at the household level, thereby observing the entire household composition of the selected households. In the long run,however, we rely in the SISBEN census of data to identify household members and toincrease statistical power. This procedure is not perfect as we can only identify school
age children residing within the household, even though they are not necessarily siblings. However, we condition on kids having the same last name to ensure that weare comparing children who either share a mother of a father and reside in the same
household.
11

This comprehensive approach allows us to assess both the short-term and longterm effects of the program on various educational outcomes of treated children andtheir siblings, such as school attendance, enrollment, high school graduation, and college enrollment and graduation.

5.5

Description of Samples

Our analysis combines four different samples that vary depending on the time of
measurement of the outcome and the type of estimated effect:
1. Direct Effects in the Short Run: This sample constitutes the entire 17,225 students
registered in the experiment.
2. Indirect Effects in the Short Run: This sample includes untreated students residing
in households with two registered students. It is considerably smaller because it
focuses on students who were part of the households included in the follow-up
survey.
3. Direct Effects in the Long Run: This is the same sample displayed in (1) and corresponds to the universe of registered students.
4. Indirect Effects in the Long Run: This sample includes untreated students residing
in households with two registered students. In this case we include that entiretyof households in the experiment and the families were identified using SISBEN.
Table 1 presents the sample sizes of our universe of analysis, by treatment status
and time of measurement of the outcome. The direct effects samples include the totality of the universe of analysis. The sample to estimate the estimates in the long runof the indirect effects limits the sample to untreated students in households with tworegistered children. The sample to estimate the short run, indirect effects, however, issmaller because it only includes the sub-group of students included in the follow up
survey.

12

Table 1: Sample Sizes in the Short and Long Run
Sample:Grades:A) San Cristóbal
Control
Basic
College
Total

Short Run
Direct Effects
Indirect Effects
6-8 9-11 Total
6-8 9-11 Total
(1)
(2)
(3)
(4) (5)(6)

Long Run
Direct Effects
Indirect Effects
6-8 9-11 Total
6-8 9-11 Total
(7)
(8)
(9)
(10) (11) (12)2,439 1,617 4,056
4,121 2,730 6,851
6,560 4,347 10,907

114
253
367

82
161
243

196
414
610

2,439 1,617 4,056
4,121 2,730 6,851
6,560 4,347 10,907

311
548
859

223
534
394
942
617 1,476

2,084 1,393
1,708- 1,133
3,792 2,526

3,477
1,708
1,133
6,318

158
79
56
293

108
56
39
203

266
135
95
496

2,084 1,393
1,708- 1,133
3,792 2,526

409
160
147
716

305
714
136
296
95
242
536 1,252

Control 4,523 3,010 7,533
Basic 5,829 2,730 8,559
College- 1,133 1,133
Total 10,352 6,873 17,225

272
332
56
660

190 462
217 5493995
446 1,106B) Suba
Control
Basic
College
Total

3,477
1,708
1,133
6,318

C) Total
4,523 3,010 7,533
5,829 2,730 8,559- 1,133 1,133
10,352 6,873 17,225

720 528 1,248
708 530 1,238
147
95
242
1,575 1,153 2,728

Note: This table displays sample sizes by site and grades in the short and long run. The estimating sample of the direct effects use
the entire universe of students in the experiment. The indirect effects sample include untreated individuals in households of two
registered children. The indirect effects sample in the short run correspond to households that were surveyed in the follow-up
survey (students registered in the 68 schools with the highest number of participants).

13

6

Reduced Form Results

6.1

Validity

We perform a balance test on multiple pre-treatment outcomes measured in thebaseline data of SISBEN. Figure 1 plots the p-values across the multiple specifications
and outcomes. As expected, due to the randomized assignment, we do not observe
consistent p-values below the pre-established critical values of 0.1 of 0.05. These tests
provide strong validity to the randomization and the causal interpretation of our results.

6.2

Treatment Effects of the Basic Arm

We estimate equation 1 to compute the short run effects of the basic treatment,
and present these results in Panel A of Table 2. We find that the basic treatment increased the likelihood of attending more than 80 percent of the classes in 0.04 percentage points and the probability of school enrollment in 0.03 percentage points. The
positive effects, however, dissipate in the long run. We do not observe any precise
point estimate among the long run outcomes, and the magnitudes are very close to
zero. These point estimates validate the results in Barrera-Osorio, Bertrand, Linden,
and Perez-Calle (2011), for the short run, and Barrera-Osorio, Linden, and Saavedra(2019) for the long run.
Despite the positive direct effects in the short run, the basic treatment had negative short and long run spillover effects on the untreated siblings of treated students.
We obtain these results by estimating equation 3 and present them in Panel B of Table
2. The untreated siblings of treated students decreased the likelihood of attending 80
percent of classes in 0.04 percentage points and of self-reporting as enrolled in 0.05
percentage points.
These spillover effects had remarkable long run repercussions in outcomes measured approximately a decade later. Even though we estimate an imprecise negative
point estimate on high school graduation, we observe a precise decrease in the probability of college enrollment of 0.05 percentage points and of college graduation in
0.03 percentage points. These are two sizable effects that imply a 12 and 30 percent
decrease in college enrolment and graduation rates, respectively.

6.3

Treatment Effects of the College Arm

The college treatment also increased attendance and enrollment among treatedchildren. We estimate equation 2 and present the results in Panel A of Table 3. We
observe a precise increase in school attendance and enrollment, and a sharp decreasein the probability of working while in school age. These positive effects translate intoa long run increase in college enrolment of 4.5 percentage points that validate what
found in Barrera-Osorio et al. (2011) and Barrera-Osorio et al. (2019).
We do not find any sizable spillover effect of the college treatment. We estimate
equation 4 and present the results in panel B of Table 3. Even though the magni14

Figure 1: Balance Across Baseline Covariates
GenderMarital Status
Single Parent HH
Age of HH headYear of Education HH head
HH Size
Number of Kids < 19Socioeconomic Stratum
SISBEN Score
HH IncomeStudent GradeHouse Ownership
Exp. Utilities
Exp. Durables
HH Infrastructure
Age at Randomization
Over Age

0 .05 .1

.2

.4

P-Value

Basic
Sibling Basic

.6

.8

1

College
Sibling College

Notes: The figures plots p-values of the point estimates across multiple specifications
using as outcomes the variables displayed in the y-axis. The direct effect of the basic
treatment is estimated using equation 1. The direct effects of the college treatment is estimated using equation 2. The indirect effect of the college treatment is estimated using
equation 3. The indirect effects of the college treatment is estimated using equation 4.
“HH” stands for households for the names displayed in the y-axis.

15

Table 2: Effects of Basic Treatment on Short and Long Run Outcomes(Estimation Point Estimates)
Short Run
Attends 80%
SchoolWorks as Primary
Enrollment
Activity
(1)
(2)
(3)
A) Direct Effects
BasicLong Run
Graduation
College
High-School Enrollment(4)(5)

Graduation
College(6)0.039***(0.010)0.031***(0.008)0.001(0.003)0.009[0.007]-0.006[0.008]0.002[0.004]

9,157
0.737

13,3930.734

8,134
0.0244

16092
0.761

16092
0.361

16084
0.0858B) Indirect Effects
Sibling Basic-0.043*(0.025)-0.054*(0.028)0.003(0.012)-0.027[0.019]-0.047**[0.020]-0.031***[0.011]

Observations
Control Mean

865
0.846

1,011
0.0346

2486
0.744

2486
0.384

2485
0.105

Observations
Control Mean

1,011
0.831

Note: This table presents the results of the estimation of equation 2 on panel A and equation 4 on panel B. The estimations inPanel B include untreated students living in households with two siblings. The indirect effects in the short term are estimatedusing the sample of students in follow-up surveys. The specification in Panel A controls for a dummy that takes the value of
one if the observation is in San Cristóbal, a dummy that takes the valus of one if the individual is in grades 6th-18, and theinteraction between these two. The specification in panel B controls for a dummy that takes the value of one if the observation
is in San Cristóbal. Panel B is estimated is the subsample of students in the follow-up survey. The outcome in column (1) is abinary variable that takes the value of one if the student attends to 80% of the classes. The outcome in column (2) corresponds toa binary variable that takes the value of one if the student self-reported as enrolled to school in the follow-up surey. The outcome
in column (3) corresponds to a binary variable that takes the value of one if the student’s main activity is to work, and is collectedin the follow-up survey. The outcome in column (4) corresponds to a binary variable that takes the value of one if the student isfound in the high shchool exit exam. The outcome in column (5) corresponds to a binary variable that takes the value of one if
the student is found in the college records. The outcome in column (6) corresponds to a binary variable that takes the value of
one if the student graduates from college. Standard errors correspond to white heteroscedastic-consistent estimates. *** p<0.01,** p<0.05, * p<0.1.

16

Table 3: Effects of College Treatment on Short and Long Run Outcomes(Validation Point Estimates)
Short Run
Attends 80%
SchoolWorks as Primary
Enrollment
Activity
(1)
(2)
(3)
A) Direct Effects
College

Observations
Control MeanB) Indirect Effects
Sibling College

Observations
Control MeanLong Run
Graduation
College
Graduation
High-School Enrollment
College
(4)
(5)
(6)

0.064***(0.025)0.042**(0.021)-0.041***(0.013)0.011[0.013]0.044**[0.020]0.016[0.015]

4,694
0.737

6,980
0.706

4,128
0.0244

8666
0.761

8665
0.361

8658
0.0858-0.053(0.052)0.043(0.043)-0.010(0.022)-0.006[0.031]

0.044[0.037]-0.002[0.024]

557
0.831

480
0.846

557
0.0346

1490
0.744

1490
0.384

1490
0.105

Note: This table presents the results of the estimation of equation 2 on panel A and equation 4 on panel B. The estimations inPanel B include untreated students living in households with two siblings. The indirect effects in the short term are estimatedusing the sample of students in follow-up surveys. The specification in Panel A controls for a dummy that takes the value of
one if the observation is in San Cristóbal, a dummy that takes the valus of one if the individual is in grades 6th-18, and theinteraction between these two. The specification in panel B controls for a dummy that takes the value of one if the observation
is in San Cristóbal. Panel B is estimated is the subsample of students in the follow-up survey. The outcome in column (1) is abinary variable that takes the value of one if the student attends to 80% of the classes. The outcome in column (2) corresponds toa binary variable that takes the value of one if the student self-reported as enrolled to school in the follow-up surey. The outcome
in column (3) corresponds to a binary variable that takes the value of one if the student’s main activity is to work, and is collectedin the follow-up survey. The outcome in column (4) corresponds to a binary variable that takes the value of one if the student isfound in the high shchool exit exam. The outcome in column (5) corresponds to a binary variable that takes the value of one if
the student is found in the college records. The outcome in column (6) corresponds to a binary variable that takes the value of
one if the student graduates from college. Standard errors correspond to white heteroscedastic-consistent estimates. *** p<0.01,** p<0.05, * p<0.1.

17

tudes of the point estimates are sizable, they are imprecise and display opposite signs.
Nonetheless, the lack of precision can be related with the small number of observations in the estimations.

7

Model

We develop a a dynamic model of household decision-making that can explain
the direct and indirect effects observed under the Basic conditional cash transfer treatment. We first set up some notation and discuss the choices available to the household. We then discuss households’ preferences, technology and optimal decisions.
The model characterizes the behavior of low-income households that have at least one
child in grades 6 to 11 in the year 2005, when randomization occurs. Some of thehouseholds have more than one child that is eligible for the program.

7.1

Notation and Environment

In t = 2005 households differ in the number of children they have and their age
structure. We let Nh,t denote the number of children household h has in period t and
we index children in each household by their birth order i = 1, 2, ..., Nh . Each childis endowed with ability ξ i,h which can be low (ξ = 0) or high (ξ = 1) with the vectorNξ h = {ξ i,h }i=1h collecting the ability endowments of all siblings. We denote by ai,h,t theage of child i, in household h as of the beginning of year t. Every child completes
grade 5 but may drop from school in subsequent grades. ei,h,t captures the completed
level of schooling for child i, in household h as of the beginning of year t. We let Kh,tdenote the set of children who are eligible for the CCT program in the sense that thatthey’ve completed grade 5 and haven’t yet completed grade 11: 5 ≤ ei,h,t < 11.
Early in t = 2005 parents in household h decide which, if any, of their eligible children i = 1, 2, ...Nh to sign up for the CCT lottery. We let indicator ℓi,h to be equal to one
when child i in household h signed up for the CCT lottery, zero otherwise. Randomization occurs among those children who sign up and individual level randomizationinduces household-level randomization. For example, a household with two childrenthat sign up for the lottery may end up with any of four possible treatments: a) both ofthem assigned to the control group, b) the first-born treated and the second one control, c) the first-born control and the second born as treated or d) both siblings treated.
Choices. Household h makes a sequence of decisions dh,t = {di,h,t } for each child ifrom ages a = 11 to 25 to maximize the presented discounted value of expected lifetime
utility. In particular, the household choices are captured by the following three 0-1
indicators• si,h,t whether child i goes to school in year t• qi,h,t whether child i attends school at least 80% of the days in year t• wa whether child i works in year t
Therefore, for each child, the household can decide whether he or she attends school,
works or stays at home, and also the level of absenteeism when he or she does attend
18

school. Attending school (with either high or low absenteeism), staying at home andworking are mutually exclusive choices.
State Variables. t(a) indexes the calendar year the child is of age a. It affects thepavailability of UCT/CCT transfers. yh,t denotes the (parental) household income, notcis the income childincluding the money that the children can get by working. yi,h,t
i gets by working in year t and Xh,t is a vector of time-varying and time-invariant
child- and household-level observable characteristics. εut is a vector capturing childand household-level unobserved heterogeneity in preferences for school attendance aswell as disutility from work/taste for leisure. εua is observed by the household before
making decisions but not by the econometrician. The vector Ωt = {t, { ai,h,t }, {ei,h,t }, Xa }collects all the observed (to both household and econometrician) state variables at timet. To simplify the exposition of the model, we let εut = {εwt , εst , εct } collect the ε that afy p yc
fect preferences and let ε t = {εut , ε t , ε t } collect all the ε, including in addition thosethat represent shocks to parental income or child income. We let χt = {Ωt , ε t , ξ } collect all state variables relevant for household decision-making, regardless of whether
they are observed by econometrician or not. In addition to keep track of the random
assignment in the RCT we let Z denote the randomly assigned group:• Control• Basic: Basic Treatment ($300,000 transfer per year)• College: College Treatment ($200,000 per year + $600,000 upon enrollment in college)
We denote by τ Z the transfer that the household receives.
Decision Horizon. Let th =t(a1,h = 11) be the first calendar year in which the household starts making decisions in our model. This is the year in which their first-born
child turns 11. Similarly, let t̄h = t(a N,h = 25) be the last calendar year in which thehousehold makes decisions in our model. This is the year in which their last-born
child turns 25. The time horizon is therefore different for each household dependingon the number of children they have and their age spacing. To capture these different
horizons, we denote by Th = t̄h − th + 1 the number of decision periods the household
has ahead of itself when it starts making decisions in the model. In the last decisionmaking period, when the youngest child reaches a = 25, the household collects a terminal value function Vt̄ (Ωt̄ ) which depends on the final school levels of all their children.
The model applies to households with children born in years t ≤ 1995 who have atleast one child between the ages of a = 11 and a = 22 in t = 2005 when recruitment for
RCT takes place. The time unit of the dynamic model is one year.

7.2

Household Preferences

Household level preferences are captured by a period utility function U(·) that depends on:• ch,t : household consumption• wi,h,t age-varying disutility from the child working• si,h,t school attendance of each child19• si,h,t−1 school attendance decisions in the previous period t − 1 to capture possible school re-entry utility costs.
• qi,h,t the level of absenteeism/presentism in the school attendance of child i.
Household utility in each period is also affected by preference shocks εU . Households
also value the final completed levels of education according to a terminal value function that, crucially depends on ei,h,t̄h , the final completed education levels of each childand possibly how unequal these are. This terminal value is denoted by Vt̄h (e1,h , e2,h , ...., e Nh ,h ; ρ).
The household takes this value in the year t̄h in which their youngest child (last-born)reaches age 25. The key structural parameter ρ, introduced in Behrman et al. (1982)
enters this terminal value function and controls the degree of parental aversion to inequality in completed education among offspring.

7.3

Household Technology

Household h can produce accumulated levels of schooling ei,h for each of theirchildren i by sending them to school and avoiding them having to work or idling at
home. Sending them to school is just a necessary condition. Actual accumulation ofcompleted levels of education will depend on the extent of their child’s absenteeism
from school. It will also depend on their child’s innate ability ξ i . We model the accumulation of completed levels of education through a grade progression probability
π. This probability for is a function of their age a, the number of completed years ofeducation e, their history of absenteeism {, their innate ability endowment ξ and otherhousehold characteristics X:
Pr (ei,h,t+1 = ei,h,t + 1 | si,h,t = 1) = πe ( aiht , eiht , {qiht }, ξ ih , Xht )7.4

Optimal Household Decisions

The problem the household solves is different before or after they are recruited into
the experiment. Before 2005, the household solves a “business-as-usual” problem. In
2005 they are surprised to learn that a CCT lottery will take place and their children are
randomized to either the control group or one of the treatment groups. Households
in which at least one child won the lottery make these subsequent choices from 2005
onward with an updated budget constraint for
To economize on notation let• sh,t = {siht }i collect all school attendance decisions in household h at time t• qh,t = ({qiht }i ) collect household absenteeism decisions for all siblings• wh,t = {wiht }i collect all child work decisions in household h at time t
Further we omit h subscript at times to simplify notation. Each household h thensolves:
( "
#)
t=t̄h

E ∑ δt−th U ct , st , s(t−1) , qt , wt ; Ωt , εut + δ Th Vt̄h (Ωt̄h ) χth
(5)
max
t=t̄

i=N

{{sit ,qit ,wit }t=th }i=1 h

t=th

20

subject top
cht = yt +i=Nh

∑ {wit × yitc + sit × 1{Zi ̸= Control} × τi (Zi , ei,t )}i=1

Pr (ei,t+1 = ei,t + 1 | si,t = 1) = πe ( ait , wit , {qit }, eit , Xt , ξ i )yppyt = y p (Xt , ε t )
yc

c
yi,t
= yc (at , et , Xt , ε it )given Pr(Xt+1 | Xt , dt )(6)
Notice that τi (Zi , ei,t ) is generic enough to capture the two types of CCT incentives
given in the “Basic” and “ College” treatments:
300, 000 if Zi = Basic and ei,t < 12
τi (Zi , ei,t ) = 200, 000 if Zi = College and ei,t < 12600, 000 if Zi = College and ei,t = 12
The sequence representation of the dynamic optimization problem described above
can re-cast into its recursive representation using a finite horizon dynamic programming formulation. Appendix C provides computational details about the recursive
representation and the algorithm used to obtain the model’s solution. After solving
the model we obtain the optimal school attendance, work and absenteeism decisions
by the household, which are a function of the state variables (Ωt , ε t , ξ) The policy functions are given by(s∗t , wt∗ , q∗t ) = dt (Ωt , ε t , ξ)

8Model Estimation

To estimate the model we follow the estimation strategy in Galiani, Pantano, andShi (2022). Functional forms associated with model implementation will be detailed inAppendix A. The ability endowment of every child ξ i is known by the household but
unobserved by the econometrician.We specify a discrete distribution of unobserved
types k = 1, ...., K N for each household size N. These types reflect the different configurations of unobserved child ability endowments ξ. For example in a two-children
household there are 4 possible types: (ξ 1 , ξ 2 ) = (0, 0), (0, 1), (1, 0), (1, 1). pk denotes theprobability that a household is of type k. These probabilities are estimated along withthe structural parameters. The joint distribution of the random vector ε is assumed to
be multivariate normal ε ∼ N(0, Σ). Appendix B provide more details.
pcParameters to be estimated are θ = {α, λe , ϕy , ϕy , ρ, Γ, pk } where α denotes parameters of the utility function, λe those in the grade progression probability function,pc
ϕy and ϕy denote, respectively, parameters in the parental and income equations, ρcaptures terminal value function parameters, Γ denotes the Cholesky Decompositionof Σ, the variance-covariance matrix of the ε and pk denote the unobserved type probK −1
abilities for k = 1, 2, 3, ..., K N where pK = 1 − ∑k=1
pk We proceed to estimation with21

a simulation-based estimation approach in the spirit of indirect inference and simulated minimum distance. Starting from an initial guess θ guess . for each vector θ ofparameters proposed in the estimation routine we repeatedly:
1. solve the model M(θ) by backwards recursion using parameters θ.
2. Use M(θ) to forward-simulate a population of households with different number of children and sibling endowed ability configurations and age spacing but
consistent with typical observed distributions in the population.
3. Consider the subset of simulated households that had at least one child potentially eligible in 2005.
4. We compute simulated moments (m(θ)) using the simulated data or subsets ofit. (some of these moments include, for example, the direct treatment effects andthe spillover effects on untreated siblings on various outcomes from the different
treatment arms. To get these we run on the simulated data the same specifications that are run in the real empirical data)
5. We compare simulated moments (m(θ)) to the analogous empirical momentsfrom the data (mdata ).
6. if distance small, stop and obtain θ̂, otherwise go to step 1 and update the guessfor θθ̂ is the vector of parameters that minimizes the distance between the empirical (mdata )and model-simulated (m(θ)) moments:
h
i′ h
i
data
data
θ̂ =θ
m
− m(θ) W m− m(θ)(7)
where W is a weight matrix. Table 2 describes the key set of moments (mdata ) to bematched in Estimation.8

9Conclusions

We examine how resource allocation within households affects parental aversion
to inequality in offspring. Theoretical work in the field highlights the fundamentalrole of household decisions in understanding economic behavior (Chiappori, 1988).
However, empirical tests of these implications have been scarce due to the challenges
in finding exogenous variation in resource allocation within the household.
In this paper, we analyze a unique setting that introduced random variation inresource allocation within households and across siblings. We study a randomized
intervention conducted in 2005 in the city of Bogotá that tested alternative delivery
methods for conditional cash transfers. The participating students were individuallyassigned to two different treatment arms, which varied the delivery methods of thetransfers. One treatment followed a standard method whereas the second prioritized
8 Appendix E will provide further detail on additional moments used for estimation22

college enrollment. Importantly, the treatment assignment was conducted at the individual level, rather than the household level. As a result, this intervention introduced
random variation in resource allocation across siblings living in the same household.
Exploiting this unique setting, we estimate both the direct treatment effects on thetreated students and the spillover effects on their untreated siblings. Our findings reveal that the conditional cash transfers improve outcomes for the directly treated students. However, the standard delivery method of the transfers has negative spillover
effects on the untreated siblings of the treated students. These results suggest thatparents reinforce within-household inequality by allocating more resources to the offspring who randomly received the transfers.
To further understand the underlying mechanisms behind these treatment effects,
we estimate a dynamic structural model. We utilize the point estimates obtained fromthe standard delivery method of the conditional cash transfers to estimate the model.
Subsequently, we validate the results of the model by comparing the true empiricalmoments of the delivery method that prioritized college enrollment with the model’s
predictions.

23

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Todd, P. and K. I. Wolpin (2006). Assessing the impact of a school subsidy program inmexico: Using a social experiment to validate a dynamic behavioral model of childschooling and fertility. American Economic Review 5(96), 1384–1417.
Todd, P. and K. I. Wolpin (2020). The best of both worlds: Combining rcts with structural modeling. Working Paper.

25

A

Functional Forms
1. Utility Function Household level preferences are captured by the period utility
function U(·) that depends on:• ch,t :household consumption• wi,h,t disutility from school-age child working• si,h,t school attendance of each child (t − 1 attendance decisions become statevariables at t to capture possible school re-entry utility costs.)• qi,h,t presentism/absenteeism of child i in household h at time t
2. Terminal Value• We specify the terminal value as function of the mean and variance of Completed Schooling as Rosenzweig and Wolpin (1988)9
ρ1 ēt̄h + ρ2 ē2t̄h + ρ3 Var(et̄h )(8)where ē is the average completed education level of all siblings and Var(e)is the variance of their completed education levels.
3. Grade Progression Probability This probability is specified as a simple logit modelof where the probability of progression (et+1 = et + 1 is a function of age a, current level of completed education e, history of absenteeism {} and unobserved
ability.
4. Income equations
yp

p

p

yp

log(yh,t ) = y p (Xt , ε h,t ) = ϕ0 + ε h,t
yc

yc

c
) = yc (at , et , Xt , ε it ) = ϕ0c + ε i,h,tlog(yi,h,t

9 Al alternative would be to use a CES as in Behrman et al. (1982)

26

B

Distributional Assumptions
 



 2
0
σ
σ
σ
σ
σ
εs
sq
sw
sp
sc
s
 0 
   σ εq 

2
σ
σ
σ
σ
qs
qw
qp
qc
 0   q   w ε  ∼ N   ,  σws σwq σw2 σwp σwc  0   yp 
   σps σpq σpw σp2 σpc 
ε 




0
c
εy i
σcs σcq σcw σcp σc20where σij = ρij × σi × σj
We will normalize some of these parameters. Following Keane and Wolpin (1994)
we use 4 + Nh standard normal random variables η ∼ N(0, I4+Nh ) and use the Cholesky
decomposition Γ of Σ where Σ = ΓΓ′ to convert the standard normal random variables
into a random vector with a joint multivariate normal distribution. We then have
Σ = Γη
Note that Γ is lower triangular with generic element γij in row i, column j so that wehave
εs = γ11 η1
εq = γ21 η1 + γ22 η2εw = γ31 η1 + γ32 η2 + γ33 η3
ε p = γ41 η1 + γ42 η2 + γ43 η3 + γ44 η4εc = γ51 η1 + γ52 η2 + γ53 η3 + γ54 η4 + γ55 η527

CModel Solution

We solve the model by backwards recursion, starting from the last year for the
youngest child and working our way back to age 11 for the oldest child, the first period we model household decisions.
At t = t̄h the alternative-specific value functions are given by
Vd (Ωt , ε t , ξ) = U(ct , d, Ω a , ξ, εut )+ Vt̄h (e1,h , e2,h , ...., e Nh ,h ; ρ)(9)At any time t < t̄h during the decision-making time span for the household, thealternative-specific value functions are given by
Vd (Ωt , ε t , ξ) = U(ct , d, Ωt , ξ, εut ) + δEΩt+1 [V(Ωt+1 , ξ)|d, Ωt , ξ ](10)where Ωt = {t, { ai,h,t }, {ei,h,t }, {di,h,t−1 }, Xt } The future component multiplying δ isgiven byEΩt+1 [V(Ωt+1 , ξ)|d, Ωt , ξ] = ∑ Pr(Ωt+1 |d, Ω a , ξ) × {V(Ωt+1 , ξ)}

(11)

Ωt+1

We use simulation-based integration to compute the EMAX terms:

V(Ωt+1 , ξ) = Eε max{Vj (Ωt+1 , ε t+1 , ξ)}

(12)

j

using the following steps:(s)• We draw S draws from the (5+N)-variate standard normal vector ηt+1 and use
the Cholesky decomposition to convert those into a vector of (5+N) correlated(s)normal random draws ε t+1 .
(s)• For each draw s, we compute all the alternative-specific value functions Vj (Ωt+1 , ε t+1 , ξ)for j ∈ J under that draw
• We take the maximum across the alternative-specific value functions(s)max{Vj (Ωt+1 , ε t+1 , ξ)}j• We then average across the S drawsV(Ωt+1 , ξ) = Eε



1 S
(s)
(13)
max{Vj (Ωt+1 , ε t+1 , ξ)} ≈ ∑ max{Vj (Ωt+1 , ε t+1 , ξ)}
S s=1
j
j


28

D

Data Details

We merge 99.31 percent of the experimental sample with the SISBEN dataset, since
the experimental households were required to have a SISBEN score in order to register. This merge provides us with first names, (two) last names, and exact date of birth
for all members of the households. Importantly, it also provides us with a permanentunique national identification number (adult id, cedula de identidad) for all membersthat are 18 years or older. This guarantees that we have no attrition among older family members.
This number, however, is not provided for household members under the age of18, but, instead, we have information on a temporary identification number (minor
id, tarjeta de identidad). We create, therefore, a cross-walk of minor to adult ids using
household location, names, date of births, and pre-existing crosswalks assembled byseveral Colombian public institution. This crosswalk allows us to recover the adult ids
of program beneficiaries and their siblings.
We then use the adult ids (if available) or names and date of births to merge to thesecondary education, tertiary education, social security, and credit access data.

29

E

Moments for Estimation and Validation• “Direct Effect” Design Moments.
• “Sibling Spillover” Design Moments.

30