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Long-Term Impacts on Education of a Cash Transfer during Early Life

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Title: Long-Term Impacts on Education of a Cash Transfer during Early Life
Language: English
Authors: Juanita Bloomfield (ORCID 0000-0002-1230-0719), José María Cabrera
Source: Journal of Policy Analysis and Management. 2026 45(1).
Availability: Wiley. Available from: John Wiley & Sons, Inc. 111 River Street, Hoboken, NJ 07030. Tel: 800-835-6770; e-mail: cs-journals@wiley.com; Web site: https://www.wiley.com/en-us
Peer Reviewed: Y
Page Count: 21
Publication Date: 2026
Document Type: Journal Articles
Reports - Research
Descriptors: Foreign Countries, Financial Support, Welfare Services, Poverty Programs, Young Children, Program Effectiveness, Educational Attainment, Body Weight, Infants
Geographic Terms: Uruguay
DOI: 10.1002/pam.22663
ISSN: 0276-8739
1520-6688
Abstract: We evaluate the long-term effects of receiving the Uruguayan "Plan de Atención Nacional a la Emergencia Social" (PANES), a large unconditional cash transfer program, on outcomes for young and unborn children. We use a rich dataset that matches program administrative data to vital natality data and educational records 8 to 12 years after the beginning of the program. Overall, we find small and barely significant effects on educational attainment and delay. Among children exposed to the program during early childhood (between ages 0 and 5), the results show significant beneficial effects for those with low birth weight.
Abstractor: As Provided
Entry Date: 2026
Accession Number: EJ1493921
Database: ERIC
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  Value: <anid>AN0190550167;jpa01jan.26;2025Dec31.04:49;v2.2.500</anid> <title id="AN0190550167-1">Long‐term impacts on education of a cash transfer during early life </title> <sbt id="AN0190550167-2">INTRODUCTION</sbt> <p>We evaluate the long‐term effects of receiving the Uruguayan Plan de Atención Nacional a la Emergencia Social (PANES), a large unconditional cash transfer program, on outcomes for young and unborn children. We use a rich dataset that matches program administrative data to vital natality data and educational records 8 to 12 years after the beginning of the program. Overall, we find small and barely significant effects on educational attainment and delay. Among children exposed to the program during early childhood (between ages 0 and 5), the results show significant beneficial effects for those with low birth weight.</p> <p>A growing literature documents that prenatal and early childhood experiences can have long‐lasting impacts on later‐life economic outcomes, human capital, health, and well‐being (Almond et al., [<reflink idref="bib2" id="ref1">2</reflink>]). In recent years, there has been a large increase in welfare programs aimed at improving conditions in early life, especially in developing countries. While it is particularly interesting for policymakers to know how effective these policies are, we are still at the beginning stages of understanding what type of intervention matters for long‐term outcomes.</p> <p>In this paper, we evaluate whether being exposed to a poverty‐alleviation program during early life has an impact on long‐term educational outcomes. We focus on the Uruguayan <emph>Plan de Atención Nacional a la Emergencia Social</emph> (PANES), a cash transfer program that was implemented between 2005 and 2007 and targeted the poorest 10% of households in the country. The program was introduced after a severe economic crisis that hit Uruguay in 2002. One special feature is that the amount of the transfer represented approximately 45% of the average household income among its target population. Although participation was announced to be conditional on school attendance for all children under age 14 and on regular health checkups for pregnant women and all children, the conditions were never enforced, so the program was de facto unconditional.</p> <p>Evaluating the long‐term effects of interventions during early childhood poses two main challenges. The first challenge is to find a credible identification strategy to evaluate the intervention. In this paper, we exploit the way in which households were assigned to the PANES program. Program assignment was determined based on a baseline predicted poverty score: Households whose score was above a certain threshold were eligible to receive the transfer. This eligibility rule generates a discontinuity that we exploit using a regression discontinuity design. We compare the educational outcomes of children belonging to households just above and just below the eligibility cutoff. We estimate impacts on three educational outcomes: highest grade attained, delay in educational attainment, and dropout.</p> <p>The second challenge in estimating long‐term effects of early childhood interventions is to find datasets that map early‐life environments to later‐life outcomes. We make use of a rich dataset that we constructed for this project, which links long‐term educational outcomes to early life experiences. Our dataset contains educational information (enrollment and grade) for the years 2013 to 2017 of eligible and ineligible children born between 2003 and 2007.</p> <p>We separately estimate the impact of the PANES program for cohorts that were exposed at different stages of early childhood. We split our analysis according to the age of the child at the onset of the program. In particular, we focus on (i) children that were between 0 and 2 years of age when the program started (born between January 2003 and March 2005), and (ii) children that were born during the program period. Therefore, given that the program ran between April 2005 and December 2007, our sample includes children who were exposed to the program between the ages of 0 and 5 (those in group [i]) and children who were exposed to the program while in‐utero and up to a maximum of 2 years and 8 months (those in group [ii]).</p> <p>Separating the analysis into children who were exposed to cash transfers since the in‐utero period and children who were exposed later in life (but still in early childhood) enables us to examine differential effects among these subgroups. On the one hand, a growing literature suggests that investments that occur during the prenatal period may potentially be more cost‐effective than postnatal interventions (Doyle et al., [<reflink idref="bib21" id="ref2">21</reflink>]). In this sense, we should expect that children who received transfers while in‐utero and after birth would benefit more from the program than those who received transfers only after birth. On the other hand, those who were exposed to the transfer later in life were born during an economic crisis and were at higher risk: The likelihood of being born with low birth weight was 0.083 in the pre‐program period, while it was 0.075 in the program period. These adversities could result in worse early child development outcomes. In this sense, additional liquidity may lead to higher effects for these children than for those born in families that started receiving the transfer during a better economic landscape. Identifying which group of children benefited more from an intervention such as PANES might help focus cash transfer policies on those children who need them most.</p> <p>Our results show that in the full sample, the PANES program produced a small and barely significant improvement in educational attainment. The effect is entirely driven by children who were born before the onset of PANES and, hence, exposed to the program during early childhood. Within this subsample, we find that children from eligible households have slightly higher educational attainment and a lower incidence of delay than ineligible children. Additionally, we find that PANES had no impact on educational dropout in the years of observation. Taken together, these findings suggest that the mild effect of PANES on educational attainment works through retention and not through dropout.</p> <p>Following Cunha and Heckman's ([<reflink idref="bib20" id="ref3">20</reflink>]) model of dynamic complementarity, one would expect that children who received transfers since the in‐utero period should have stronger effects on education than those who received them only after birth. However, our findings show the opposite: The effect of the PANES program on education is driven by children exposed to the program during early childhood (and after birth). Because this group was born in a worse economic environment, our interpretation is that the transfers have a stronger effect on education for children who are born with more risk. We further explore this issue by estimating heterogeneous effects by low birth weight status among children born in the pre‐program period. We find that the effects of PANES on educational attainment are stronger among children born with low birth weight.</p> <p>We find no effects of PANES on the long‐term educational results of children who were in their mothers' wombs during the program period. Given previous evidence showing that the PANES program improved health at birth as measured by birth weight (Amarante et al., [<reflink idref="bib5" id="ref4">5</reflink>]) and the importance of health at birth for later educational outcomes, this finding seems surprising. However, when we estimate the effect of PANES on health at birth, we find no significant effects. Our findings differ from those in Amarante et al. ([<reflink idref="bib5" id="ref5">5</reflink>]) because we use a different identification strategy and a different dataset.</p> <p>Cash transfers were established with the aim of alleviating household financial restrictions. Some variations of these programs impose conditionalities on school attendance to promote human capital accumulation and break the intergenerational transmission of poverty. Such is the case of Mexico's well‐known Progresa, one of the earliest conditional cash transfer programs. Progresa began in 1997 and consisted of regular cash transfers to women conditional on human capital investments, including visits to healthcare providers for young children, and school enrollment and attendance for school‐age children. The program increased school enrollment and attendance after its first 18‐month randomized evaluation (Parker & Todd, [<reflink idref="bib34" id="ref6">34</reflink>]). Due in large part to Progresa's results, conditional cash transfers have become common in Latin America and have spread to other parts of the world. A large body of evidence has found that these interventions have positive effects on schooling while impacts on employment and earnings are mixed (see Millán et al., [<reflink idref="bib32" id="ref7">32</reflink>], for a review). The positive impacts during early adulthood of childhood exposure to Progresa are mostly concentrated among women (Parker & Vogl, [<reflink idref="bib35" id="ref8">35</reflink>]).</p> <p>Unconditional cash transfers are not tied to any particular behavior and thus provide cash payments to everyone in the eligible target population. The number of studies assessing unconditional cash transfers on schooling is substantially smaller than those analyzing transfers that impose conditionalities, but it is growing. Unconditional cash transfers have been shown to increase enrollment in education in the short run (Baird et al., [<reflink idref="bib9" id="ref9">9</reflink>]), as well as household consumption (Haushofer & Shapiro, [<reflink idref="bib26" id="ref10">26</reflink>]), but their effectiveness in improving outcomes associated with conditions is inferior relative to conditional cash transfers (Baird et al., [<reflink idref="bib10" id="ref11">10</reflink>]). Moreover, there is evidence that while unconditional cash transfers improve immediate welfare, additional interventions are necessary for lasting poverty reductions (Handa et al., [<reflink idref="bib25" id="ref12">25</reflink>]).</p> <p>Longer‐term analyses are especially important for cash transfers since these programs aim to reduce future poverty by augmenting the human‐capital levels of children and youth from poor families. However, while there is sufficient evidence of the impact of cash transfer interventions in the short run (Fiszbein & Schady, [<reflink idref="bib23" id="ref13">23</reflink>]), the evidence on long‐run effects is sparse (Millán et al., [<reflink idref="bib32" id="ref14">32</reflink>]). In the case of randomized evaluations, for example, high rates of migration make following up samples expensive and complicated. Millán et al. ([<reflink idref="bib32" id="ref15">32</reflink>]) claimed that the measurement of long‐term impacts using rigorous identification strategies should be high on the research agenda.</p> <p>Overall, the sparse evidence on the long‐term effects of unconditional cash transfers shows no or little effect on education. Two examples from the African context are Haushofer and Shapiro ([<reflink idref="bib27" id="ref16">27</reflink>]) and Blattman et al. ([<reflink idref="bib17" id="ref17">17</reflink>]). The former evaluated an unconditional cash transfer in Kenya 3 years after the beginning of the program, and the latter evaluated the effectiveness of cash grants in Uganda 9 years after the implementation of the program.</p> <p>In Uruguay, the PANES program has been evaluated on a range of short‐term outcomes such as school attendance, labor supply, political support, and birth weight. Overall, studies have found that the program had no impact on child labor or school attendance for children aged 14 to 17 (Amarante et al., [<reflink idref="bib4" id="ref18">4</reflink>]), decreased formal labor supply (Amarante et al., [<reflink idref="bib6" id="ref19">6</reflink>]), increased political support for the current government relative to the previous government (Manacorda et al., [<reflink idref="bib30" id="ref20">30</reflink>]), and improved health at birth outcomes (Amarante et al., [<reflink idref="bib5" id="ref21">5</reflink>]).</p> <p>Our paper contributes to the literature in two ways. First, we contribute to a growing body of work on the medium‐ to long‐term effects of (unconditional) cash transfer programs in developing countries. We measure educational outcomes 8 to 12 years after exposure, a longer period than that in most other studies. Moreover, we study the case of Uruguay, a middle‐income country in Latin America whose population and economic setting are very different from those in Africa. Second, a novel angle of the paper rests on the age of the children considered. We focus on the effects of the program since the in‐utero period and up to 5 years of age. The evidence base for exposure in early childhood is more limited than for exposure during school‐going ages (Millán et al., [<reflink idref="bib32" id="ref22">32</reflink>]). Recent evidence has shown positive effects of cash transfers following the birth of a child on earnings and education (Barr et al., [<reflink idref="bib12" id="ref23">12</reflink>]). We consider the long‐term effect of cash transfers on education from an even earlier stage: the in‐utero period. In this way, we provide evidence to complement the findings in Araujo and Macours ([<reflink idref="bib8" id="ref24">8</reflink>]), the first long‐term evaluation of a cash transfer implemented at scale during the first 1,000 days of life.</p> <p>Beyond the cash transfer literature, this paper relates to the literature that links resources in‐utero to educational outcomes later in life. While most other studies have focused on long‐term effects of negative shocks such as famines, disease, and radiation (see Almond et al., [<reflink idref="bib2" id="ref25">2</reflink>], for a recent review), we focus on a policy that implies a positive treatment.</p> <p>The remainder of this paper is structured as follows. The section "The PANES Program" describes the PANES program. The sections "Data" and "Empirical Framework" describe the data and empirical framework, respectively. "Empirical Results" reports results of the effect of the PANES program on educational outcomes and low birth weight. Finally, "Discussion" provides a discussion of the findings.</p> <hd id="AN0190550167-3">THE PANES PROGRAM</hd> <p>The <emph>Plan de Atención Nacional a la Emergencia Social</emph> (PANES) was a temporary social assistance program that ran from April 2005 to December 2007 in Uruguay, a middle‐income country in Latin America. The program targeted the poorest households in the country. PANES was designed as an emergency plan to alleviate material hardship caused by a severe economic crisis that hit Uruguay in 2002 and was among the flagship policies of the center‐left government that took office in March 2005. The Ministry for Social Development (<emph>Ministerio de Desarrollo Social</emph>) was created to oversee the implementation of the program.</p> <p>Program eligibility was based on families' scores on a poverty index. All applicant households were visited by personnel from the Ministry of Social Development and completed a detailed baseline survey, which allowed program officials to compute the score. The score depended on many household socioeconomic characteristics and was based on a probit model of the likelihood of being below a per capita income level using a highly saturated function of household variables (Amarante et al., [<reflink idref="bib3" id="ref26">3</reflink>]). The estimation of the underlying model was performed using the 2003 and 2004 National Household Survey (<emph>Encuesta Continua de Hogares</emph>), and the resulting coefficient estimates were used to predict a score value for each applicant using PANES baseline survey data. Appendix Tables A1 and A2 provide further information on the variables used to predict the poverty score. The variables considered, the weights attached to the observed covariates, and the eligibility thresholds varied slightly across different geographic regions. Applicants were not aware of the variables that entered the score, the weights attached to them, or the eligibility criteria, easing concerns about manipulation of the score.</p> <p>Rather than using actual reported income, the score was estimated using a wide range of socioeconomic variables. This approach was adopted because the program's target population often worked in the informal sector, making it difficult to verify self‐reported income. By using indirect measures of income, the possibility of strategic misreporting was minimized.</p> <p>Around 188,671 households (with approximately 700,000 individuals) submitted applications. After the interviewing process, households were ranked according to their level of deprivation based on their predicted poverty score. Households whose score was above a predetermined threshold were assigned to the program. About 54% of applicant households became beneficiaries, representing nearly 10% of households in the country. Regardless of their characteristics, eligible households received a monthly cash transfer that initially amounted to $1,360 Uruguayan pesos (US$102 adjusted by PPP). This amount was adjusted for inflation on a quarterly basis. The transfer corresponded to approximately 45% of the average household income among the poorest 10% of households in Uruguay.<sups>,</sups></p> <p>The condition for continuing to receive the payment was that household income (from all sources) remained below a specific per capita level. In practice, only verifiable sources of income were taken into account. Successive checks were carried out by the social security administration to enforce this condition, and because of this, some households stopped receiving the transfer before the end of the program. There were no other formal conditionalities (such as health checks for children and pregnant women or school attendance for children) until mid‐2007, and even then, conditionalities were never enforced.</p> <p>The program included several components. The main element was the monthly cash transfer (<emph>ingreso ciudadano</emph>, "citizen income"). Midway through the program, an electronic food card (<emph>tarjeta alimentaria</emph>) was introduced, and households with children or pregnant women were entitled to receive it in addition to the cash transfer. The food card operated through an electronic debit card, and its value represented between 22% and 59% of the value of the income transfer, depending on household size and demographic structure.</p> <p>On an annual basis, the program's cost was 0.41% of GDP. The program ended in December 2007, and the target population, eligibility rules, and assistance levels changed when a new cash transfer and health care reform (<emph>Plan de Equidad</emph>) was launched in January 2008. Households did not need to reapply for the new program. The government informed households about the end of PANES and the start of the new program via mail, and eligible households received a formal written communication. Eligibility for the <emph>Plan de Equidad</emph> was based on a new score estimated for all original PANES applicant households using the same baseline characteristics registered in 2005 but with a new formula. The threshold for program eligibility changed from PANES; it became less restrictive and expanded the beneficiary base. Members from both eligible and ineligible households in PANES became eligible for the new program. In 79% of PANES applicant households, at least one household member became eligible for the <emph>Plan de Equidad</emph>. Further in the paper, we show that we do not find significant differences in the probability that at least one household member received the <emph>Plan de Equidad</emph> when considering households that are close to the PANES eligibility threshold (see Table 3). It is important to note, however, that in this paper we estimate the marginal effect of receiving the PANES program on top of receiving future cash transfers from the <emph>Plan de Equidad</emph>. In this sense, our analysis resembles previous studies on Progresa in Mexico, which evolved into Oportunidades and later into Prospera (Araujo & Macours, [<reflink idref="bib8" id="ref27">8</reflink>]).</p> <hd id="AN0190550167-4">DATA</hd> <p>We use a rich dataset that links administrative records from three governmental sources. All sources contain information at the individual level, and we use de‐identified identity numbers to match these three sources. In this section, we describe the data sources used and provide descriptive statistics.</p> <hd id="AN0190550167-5">Data sources</hd> <p></p> <hd id="AN0190550167-6">Data from the Ministry of Social Development</hd> <p>Our primary source is the administrative records of the initial baseline survey visit for both successful and unsuccessful female applicants in PANES. The Ministry of Social Development (<emph>Ministerio de Desarrollo Social</emph>, MIDES) shared with us the responses to the comprehensive questionnaire applied by MIDES agents during the visits. Some households submitted more than one application to the program, but we retained information only from the first visit to ease concerns about strategic behaviors to gain eligibility. The key variables we use from this source are the household's exact predicted poverty score and an indicator for approval in PANES. We also use information on the household's sociodemographic characteristics, housing conditions, and durable asset ownership.</p> <hd id="AN0190550167-7">Birth data</hd> <p>We combine information from PANES administrative records with all registered live births in Uruguay from birth certificates (<emph>Certificado de Nacido Vivo</emph>) for the period 2003 to 2007. The latter are registered by the Statistical Office of the Ministry of Health (<emph>Ministerio de Salud Pública</emph>). Birth certificates have unique identification numbers for mothers, which we used to match them with females in PANES applicant households. However, the identity numbers of children were not available in birth certificates. To obtain this information, we used additional records from MIDES that contain identification numbers of mothers and children who applied for or received any social program. We matched this dataset with PANES records using the mother's identification number and the date of birth. For multiple births of the same gender, it was not possible to determine which identification number corresponded to each child. Because this information was crucial for linking birth data with education data, we had to drop observations from multiple births (1% of the sample). The vital statistics natality data includes information on health at birth, the mother's reproductive history, parental characteristics, and prenatal health care utilization.</p> <hd id="AN0190550167-8">Education data</hd> <p>Finally, we use children's identification numbers to obtain information on enrollment by year and grade from administrative data registered by the Statistical Office of the National Administration of Public Education (<emph>Administración Nacional de Educación Pública</emph>). We have data for the years 2013 to 2017, corresponding to 8 to 12 years after the beginning of the PANES program. For each year, we know the grade in which the child was enrolled, but not whether the grade was completed in that particular year. With this data, we constructed three outcome variables for our analysis: highest grade attained, delay, and dropout in education. The highest grade attained corresponds to the grade the child had reached by 2017, the last year for which we have information, and ranges from 1 to 10, with 1 being preschool and 10 the last year of middle school. If the child's record is missing in 2017, we take the highest grade attained by the child in the period we observe her. Delay is measured with an indicator that takes value 1 if the child's highest grade attained in 2017 is lower than the one determined by her year and month of birth and a regular track. Appendix Table A3 shows the corresponding grade that a child should have attained in 2017 according to their year and month of birth. Dropout is an indicator that takes the value 1 if the child was not enrolled in education for 2 or more years during the period we observe her.</p> <p>The three outcomes we consider capture different elements of students' educational careers. The highest grade attained shows the overall educational attainment of the child. Delay adds to the latter by also considering information on the year and month of birth of the child. There are two possible explanations for why a child may be enrolled at a lower grade than expected based on her age and a regular track: (i) the child repeated a grade, or (ii) the child did not enroll in school for some years. We explore the possibility of explanation (ii) using a variable that indicates whether the child dropped out of school for two or more years during the period we observe her.</p> <hd id="AN0190550167-9">Descriptive statistics</hd> <p>Overall, we have information on 49,062 mothers and 59,128 children. Almost half of the children in our sample (49%) were born during the program period. Table 1 presents descriptive statistics of our outcome variables and selected covariates for children born in the pre‐program period (January 2003 to March 2005) and children born in the program period (April 2005 to December 2007). There is a difference in educational outcomes measured 8 to 12 years after exposure to the program between eligible and ineligible groups. For example, considering the highest grade attained, children born in non‐eligible households in the pre‐program period attained 8 years of education, while eligible children born in the same period attained 7.6 years. Children born during the program period attain lower levels of education than children born in the pre‐program period because they are younger at the time we observe them. Non‐eligible children born after the beginning of the program attain, on average, 5.8 years of education, while eligible children attain 5.7 years.</p> <p>1 TABLE Descriptive statistics of outcome variables and selected covariates.</p> <p> <ephtml> <table><thead><tr><th /><th align="center">Eligible households</th><th align="center">Non eligible households</th><th align="center">Difference</th></tr><tr><th /><th><italic>N</italic></th><th align="center">Mean</th><th align="center">Std. dev.</th><th><italic>N</italic></th><th align="center">Mean</th><th align="center">Std. dev.</th><th align="center">Coefficient</th><th align="center">s.e.</th></tr></thead><tbody><tr><td>Panel A: Born in pre‐program period</td><td /><td /><td /><td /><td /><td /><td /><td /></tr><tr><td>Child's highest grade attained</td><td>22157</td><td>7.758</td><td>1.016</td><td>6751</td><td>7.975</td><td>1.006</td><td>−0.217<ext-link /><sup>***</sup></td><td>(0.014)</td></tr><tr><td>Delay</td><td>22157</td><td>0.602</td><td>0.490</td><td>6751</td><td>0.482</td><td>0.500</td><td>0.120<ext-link /><sup>***</sup></td><td>(0.007)</td></tr><tr><td>Dropout</td><td>22157</td><td>0.025</td><td>0.156</td><td>6751</td><td>0.031</td><td>0.172</td><td>−0.006<ext-link /><sup>**</sup></td><td>(0.002)</td></tr><tr><td>Mother's number of previous pregnancies</td><td>22157</td><td>3.381</td><td>2.310</td><td>6751</td><td>2.362</td><td>1.662</td><td>1.019<ext-link /><sup>***</sup></td><td>(0.030)</td></tr><tr><td>Mother's age at birth</td><td>21778</td><td>25.432</td><td>6.727</td><td>6667</td><td>24.433</td><td>6.445</td><td>0.998<ext-link /><sup>***</sup></td><td>(0.093)</td></tr><tr><td>Child's birth weight (BW) in grams</td><td>22000</td><td>3175.765</td><td>516.708</td><td>6696</td><td>3199.972</td><td>518.474</td><td>−24.206<ext-link /><sup>***</sup></td><td>−7.217</td></tr><tr><td>Child has low birth weight (=1 if BW <2500 grams)</td><td>22000</td><td>0.087</td><td>0.282</td><td>6696</td><td>0.079</td><td>0.269</td><td>0.008<ext-link /><sup>**</sup></td><td>(0.004)</td></tr><tr><td>Gestational week of birth occurrence</td><td>21512</td><td>38.637</td><td>1.728</td><td>6581</td><td>38.647</td><td>1.783</td><td>−0.010</td><td>(0.025)</td></tr><tr><td>Child was born premature (=1 if gestational weeks <37)</td><td>21512</td><td>0.082</td><td>0.275</td><td>6581</td><td>0.081</td><td>0.273</td><td>0.001</td><td>(0.004)</td></tr><tr><td>Child's Apgar score 1 minute</td><td>21923</td><td>8.535</td><td>1.035</td><td>6709</td><td>8.550</td><td>0.999</td><td>−0.015</td><td>(0.014)</td></tr><tr><td>Child's Apgar score 5 minutes</td><td>21929</td><td>9.642</td><td>0.791</td><td>6708</td><td>9.649</td><td>0.742</td><td>−0.007</td><td>(0.011)</td></tr><tr><td>Mother's number of prenatal controls</td><td>21940</td><td>6.560</td><td>3.366</td><td>6678</td><td>7.560</td><td>3.166</td><td>−0.961<ext-link /><sup>***</sup></td><td>(0.046)</td></tr><tr><td>Panel B: Born during program period</td><td /><td /><td /><td /><td /><td /><td /><td /></tr><tr><td>Child's highest grade attained</td><td>22221</td><td>5.717</td><td>1.049</td><td>7999</td><td>5.823</td><td>1.009</td><td>−0.106<ext-link /><sup>***</sup></td><td>(0.014)</td></tr><tr><td>Delay</td><td>22221</td><td>0.382</td><td>0.486</td><td>7999</td><td>0.284</td><td>0.451</td><td>0.097<ext-link /><sup>***</sup></td><td>(0.006)</td></tr><tr><td>Dropout</td><td>22221</td><td>0.020</td><td>0.141</td><td>7999</td><td>0.032</td><td>0.176</td><td>−0.012<ext-link /><sup>***</sup></td><td>(0.002)</td></tr><tr><td>Mother's number of previous pregnancies</td><td>22221</td><td>3.396</td><td>2.344</td><td>7999</td><td>2.422</td><td>1.590</td><td>0.974<ext-link /><sup>***</sup></td><td>(0.028)</td></tr><tr><td>Mother's age at birth</td><td>21772</td><td>25.124</td><td>6.824</td><td>7873</td><td>24.675</td><td>6.386</td><td>0.449<ext-link /><sup>***</sup></td><td>(0.088)</td></tr><tr><td>Child's birth weight (BW) in grams</td><td>22012</td><td>3214.934</td><td>522.616</td><td>7925</td><td>3225.874</td><td>525.796</td><td>−10.940</td><td>−6.857</td></tr><tr><td>Child has low birth weight (=1 if BW <2500 grams)</td><td>22012</td><td>0.077</td><td>0.266</td><td>7925</td><td>0.074</td><td>0.262</td><td>0.003</td><td>(0.003)</td></tr><tr><td>Gestational week of birth occurrence</td><td>21353</td><td>38.648</td><td>1.694</td><td>7654</td><td>38.664</td><td>1.686</td><td>−0.015</td><td>(0.023)</td></tr><tr><td>Child was born premature (=1 if gestational weeks <37)</td><td>21353</td><td>0.079</td><td>0.269</td><td>7654</td><td>0.078</td><td>0.268</td><td>0.001</td><td>(0.004)</td></tr><tr><td>Child's Apgar score 1 minute</td><td>22005</td><td>8.538</td><td>0.980</td><td>7925</td><td>8.516</td><td>0.999</td><td>0.021<ext-link /><sup>*</sup></td><td>(0.013)</td></tr><tr><td>Child's Apgar score 5 minutes</td><td>22004</td><td>9.651</td><td>0.713</td><td>7925</td><td>9.641</td><td>0.709</td><td>0.010</td><td>(0.009)</td></tr><tr><td>Mother's number of prenatal controls</td><td>21887</td><td>6.777</td><td>3.368</td><td>7869</td><td>7.728</td><td>3.132</td><td>−0.951<ext-link /><sup>***</sup></td><td>(0.043)</td></tr></tbody></table> </ephtml> </p> <p>1 <emph>Notes</emph>: Standard errors (s.e.) are reported in parentheses. <emph>N</emph> corresponds to number of observations. Std. dev. corresponds to standard deviation. † The Apgar score is a widely accepted method for assessing a newborn's condition right after birth and gauging the effectiveness of any resuscitation efforts, maintaining its status as the benchmark for neonatal evaluation. It is assessed at two different times after birth: at 1 minute and at 5 minutes. In summary, the 1‐minute Apgar score focuses on the neonate's immediate response to birth, while the 5‐minute score assesses how the baby is adapting to life outside the womb and the effectiveness of any resuscitative efforts. Higher values represent better health conditions.</p> <p>2 <sups>*</sups><emph>p</emph> < .1, <sups>**</sups><emph>p</emph> < .05, <sups>***</sups><emph>p</emph> < .01.</p> <p>There is also a difference in the incidence of low birth weight between eligible and ineligible households. In the pre‐program period, 8.7% of eligible children were born with low birth weight, while among ineligible children, the incidence was 7.9%. During the program period, the gradient in low birth weight is less pronounced (7.7% and 7.4% for eligible and ineligible households, respectively).</p> <hd id="AN0190550167-10">EMPIRICAL FRAMEWORK</hd> <p>In this section, we explain the main identification strategy used to estimate the impacts of the PANES program on long‐term educational results. We also present first‐stage estimates of the effect of eligibility for the PANES transfer on actual treatment and discuss the validity of our main estimates.</p> <hd id="AN0190550167-11">Identifying long‐run impacts of the PANES program</hd> <p>To examine the impact of the PANES program on educational attainment 8 to 12 years after exposure to the program, we use a regression discontinuity design (RDD). This approach takes advantage of the fact that program assignment was determined by a predicted poverty score. Families with a score above a certain threshold were eligible to receive the cash transfer, while those below the threshold were not. This rule creates a discontinuity in the probability of receiving the transfer at the threshold, which we exploit to identify the causal effects of the program. Given that eligibility enforcement is high but not perfect, we estimate program effects using a fuzzy regression discontinuity design.</p> <p>We compare educational outcomes of children born to households that were just above and just below the threshold. The intuition behind this approach is that households near the cutoff are likely to be similar in all respects except for their treatment status, which is quasi‐randomly assigned. Therefore, any significant differences in educational outcomes between the two groups can be attributed to the effect of the PANES program.</p> <p>The equation we estimate is: 1 <ephtml> <math display="block" altimg="urn:x-wiley:02768739:media:pam22663:pam22663-math-0001" xmlns="http://www.w3.org/1998/Math/MathML"><semantics><mrow><msub><mi>Y</mi><mrow><mi>i</mi><mi>m</mi><mi>t</mi></mrow></msub><mo linebreak="badbreak">=</mo><msub><mi>α</mi><mn>0</mn></msub><mo linebreak="goodbreak">+</mo><msub><mi>α</mi><mn>1</mn></msub><msub><mi>T</mi><mi>m</mi></msub><mo linebreak="goodbreak">+</mo><mi>f</mi><mfenced separators="" open="(" close=")"><msub><mi>N</mi><mi>m</mi></msub></mfenced><mo linebreak="goodbreak">+</mo><msub><mi>α</mi><mn>2</mn></msub><msub><mi>X</mi><mrow><mi>i</mi><mi>m</mi><mi>t</mi></mrow></msub><mo linebreak="goodbreak">+</mo><msub><mi>e</mi><mrow><mi>i</mi><mi>m</mi><mi>t</mi></mrow></msub></mrow><annotation encoding="application/x-tex">$$\begin{equation}{{Y}_{imt}} = {{\alpha }_0} + {{\alpha }_1}{{T}_m} + f\left({{{N}_m}} \right) + {{\alpha }_2}{{X}_{imt}} + {{e}_{imt}}\end{equation}$$</annotation></semantics></math> </ephtml> where <emph>Y</emph> represents the schooling outcome of interest for child <emph>i</emph> conceived by mother <emph>m</emph> and born in year <emph>t</emph>, T<subs>m</subs> is a binary indicator variable that takes the value 1 if the mother <emph>m</emph> received the benefit or 0 otherwise, N<subs>m</subs> denotes mother <emph>m</emph>'s predicted poverty score (normalized relative to the eligibility threshold such that households with positive N<subs>m</subs> are eligible for treatment), <emph>f</emph> is a function of the running variable that is continuous at the threshold (N<subs>m</subs> = 0) and that may have different slopes at each side of the cutoff. All regressions control for month times year of birth fixed effects, and month times year of baseline visit fixed effects.X<subs>imt</subs> include the latter fixed effects and may also include other controls as we mention in the following paragraph. e<subs>imt</subs> is a random error term. We instrument the PANES treatment variable T<subs>m</subs>, with an indicator for the mother's program eligibility, E<subs>m</subs>. <emph>α</emph><subs>1</subs> is the parameter of interest.</p> <p>As in fully randomized experiments, it is not necessary to include covariates in regression discontinuity designs. However, it is common to include them to reduce variability in the estimation (Lee & Lemieux, [<reflink idref="bib29" id="ref28">29</reflink>]). In our estimations, we control for covariates, X<subs>imt</subs>, at the levels of the child, mother, and household. Controls are included as indicator variables, and we use a separate category for missing observations in each control.</p> <p>We estimate equation (<reflink idref="bib1" id="ref29">1</reflink>) for the entire sample and two subsamples: children exposed to the cash transfer while in utero (i.e., those born between April 2005 and December 2007) and children exposed to the cash transfer after birth (i.e., those born between January 2003 and March 2005). We report conventional point estimates combined with robust standard errors, based on the bandwidth and polynomial selected following the approach of Calonico et al. ([<reflink idref="bib19" id="ref30">19</reflink>]). This approach involves a local polynomial nonparametric estimator with a data‐driven bandwidth selector and bias‐correction techniques. We refer to this method as "CCT." In most cases, the optimal bandwidth ranges between 0.05 and 0.1, corresponding to differences of 5 to 10 percentage points in the predicted poverty score.</p> <p>To account for multiple hypotheses across outcomes and sub‐populations, we also report the sharpened <emph>q</emph>‐values proposed by Benjamini and Hochberg ([<reflink idref="bib15" id="ref31">15</reflink>]), which control for the false discovery rate. We group highest grade attained and delay together in one family of outcomes and dropout in another. For the sake of brevity, we report <emph>q</emph>‐values only for statistically significant estimates that inform our main results.</p> <p>One concern is that pregnancy might be endogenous to gaining program eligibility. Having one more child would increase the probability of treatment since the score was estimated using the <emph>per capita</emph> income level of the household. This could bias the estimates of program impact if women who change their pregnancy patterns give birth to children with different characteristics, such as a different probability of low birth weight. Given that the initial application period was concentrated in a relatively short timeframe (75% of applications occurred in the first 9 months of the program), it seems unlikely that fertility patterns were influenced in such a period. A related issue is the possibility of fertility responses to the program to retain eligibility. To mitigate concerns about subsequent fertility choices, we use the predicted income score at the initial application as an instrument for program receipt, rather than the score at each reassessment of eligibility status, where household circumstances, including childbirth, may have changed.</p> <hd id="AN0190550167-12">First‐stage effects of the PANES program</hd> <p>Figure 1 shows a clear jump in the fraction of individuals who actually received the PANES transfers. While 96% of poor households located to the right of the cutoff received the cash transfer, 13% of ineligible households managed to enter the program.</p> <p> <img src="https://imageserver.ebscohost.com/img/embimages/rdk/JPA/01jan26/pam22663-fig-0001.jpg?ephost1=dGJyMNXb4kSepq84yOvqOLCmsE6epq5Srqa4SK6WxWXS" alt="pam22663-fig-0001.jpg" title="1 Receipt of PANES. [Colour figure can be viewed at wileyonlinelibrary.com]Notes: The vertical line corresponds to the eligibility cutoff, above which households are eligible to the program and below which they are not eligible to the program. There are 10 bins at each side of the cutoff and the range is −0.1, 0.1. Each dot represents the fraction of households that received the PANES transfers in that bin." /> </p> <p></p> <p>Table 2 presents first‐stage estimates of the effect of eligibility for the PANES transfer on actual treatment. We report results using three different ranges around the eligibility threshold (columns 1 through 8). In columns 13 and 14 we also report results for the bandwidth defined according to Calonico et al. ([<reflink idref="bib19" id="ref32">19</reflink>]). In Panel A, we report estimates for the whole sample; in Panel B, we report estimates for children exposed during early childhood; and in Panel C, we report estimates for those exposed while in utero. The estimated increase in the fraction of treated households at the threshold is substantial (between 0.70 and 0.76) and remains consistent across specifications. The first‐stage estimates become larger when using observations that are further away from the cutoff.</p> <p>2 TABLE First stage estimates of the effect of the eligibility on the PANES cash transfer.</p> <p> <ephtml> <table><thead><tr><th /><th align="center">(1)</th><th align="center">(2)</th><th align="center">(3)</th><th align="center">(4)</th><th align="center">(5)</th><th align="center">(6)</th><th align="center">(7)</th><th align="center">(8)</th></tr></thead><tbody><tr><td>Panel A: All observations</td><td /><td /><td /><td /><td /><td /><td /><td /></tr><tr><td>Coefficient</td><td>0.747<ext-link /><sup>***</sup></td><td>0.755<ext-link /><sup>***</sup></td><td>0.741<ext-link /><sup>***</sup></td><td>0.747<ext-link /><sup>***</sup></td><td>0.701<ext-link /><sup>***</sup></td><td>0.717<ext-link /><sup>***</sup></td><td>0.702<ext-link /><sup>***</sup></td><td>0.716<ext-link /><sup>***</sup></td></tr><tr><td>s.e.</td><td>(0.007)</td><td>(0.007)</td><td>(0.008)</td><td>(0.008)</td><td>(0.010)</td><td>(0.010)</td><td>(0.013)</td><td>(0.012)</td></tr><tr><td>Observations</td><td align="center">25622</td><td align="center">25622</td><td align="center">19863</td><td align="center">19863</td><td align="center">13262</td><td align="center">13262</td><td align="center">9358</td><td align="center">9592</td></tr><tr><td>Range</td><td>0.1</td><td>0.1</td><td>0.075</td><td>0.075</td><td>0.05</td><td>0.05</td><td>0.036</td><td>0.037</td></tr><tr><td>Panel B: Exposed during early‐childhood</td><td /><td /><td /><td /><td /><td /><td /><td /></tr><tr><td>Coefficient</td><td>0.742<ext-link /><sup>***</sup></td><td>0.757<ext-link /><sup>***</sup></td><td>0.736<ext-link /><sup>***</sup></td><td>0.750<ext-link /><sup>***</sup></td><td>0.697<ext-link /><sup>***</sup></td><td>0.720<ext-link /><sup>***</sup></td><td>0.693<ext-link /><sup>***</sup></td><td>0.718<ext-link /><sup>***</sup></td></tr><tr><td>s.e.</td><td>(0.010)</td><td>(0.010)</td><td>(0.012)</td><td>(0.011)</td><td>(0.014)</td><td>(0.014)</td><td>(0.019)</td><td>(0.018)</td></tr><tr><td>Observations</td><td align="center">12198</td><td align="center">12198</td><td align="center">9435</td><td align="center">9435</td><td align="center">6277</td><td align="center">6277</td><td align="center">5119</td><td align="center">5156</td></tr><tr><td>Range</td><td>0.1</td><td>0.1</td><td>0.075</td><td>0.075</td><td>0.05</td><td>0.05</td><td>0.042</td><td>0.042</td></tr><tr><td>Panel C: Exposed while in‐utero</td><td /><td /><td /><td /><td /><td /><td /><td /></tr><tr><td>Coefficient</td><td>0.751<ext-link /><sup>***</sup></td><td>0.754<ext-link /><sup>***</sup></td><td>0.744<ext-link /><sup>***</sup></td><td>0.747<ext-link /><sup>***</sup></td><td>0.703<ext-link /><sup>***</sup></td><td>0.715<ext-link /><sup>***</sup></td><td>0.707<ext-link /><sup>***</sup></td><td>0.710<ext-link /><sup>***</sup></td></tr><tr><td>s.e.</td><td>(0.009)</td><td>(0.009)</td><td>(0.011)</td><td>(0.011)</td><td>(0.014)</td><td>(0.013)</td><td>(0.019)</td><td>(0.018)</td></tr><tr><td>Observations</td><td align="center">13424</td><td align="center">13424</td><td align="center">10428</td><td align="center">10428</td><td align="center">6985</td><td align="center">6985</td><td align="center">5066</td><td align="center">5053</td></tr><tr><td>Range</td><td>0.1</td><td>0.1</td><td>0.075</td><td>0.075</td><td>0.05</td><td>0.05</td><td>0.037</td><td>0.037</td></tr><tr><td>Controls</td><td align="center">No</td><td align="center">Yes</td><td align="center">No</td><td align="center">Yes</td><td align="center">No</td><td align="center">Yes</td><td align="center">No</td><td align="center">Yes</td></tr></tbody></table> </ephtml> </p> <ulist> <item>3 <emph>Notes</emph>: Each cell corresponds to a different regression. In columns 1 through 6 we estimate equation (<reflink idref="bib1" id="ref33">1</reflink>) using as outcome variable an indicator that takes the value of one if the household received the PANES transfer. We report results for three different fixed ranges around the eligibility threshold and a first order polynomial. We also report the estimates obtained when using the bandwidth and polynomial defined according to Calonico et al. ([<reflink idref="bib19" id="ref34">19</reflink>]). (See Columns 7 and 8.) All estimations include month times year of birth fixed effects, and month times year of baseline visit fixed effects. Estimations in even columns we include the following additional controls: gender of the child, an indicator for whether the mother completed primary school, number of bedrooms in the household and indicators for whether the household's block has sewage and trash collection. All controls are included as indicator variables and include a category for missing observations. Standard errors (s.e.) are reported in parentheses and number of observations are reported below each coefficient.</item> <item>4 <sups>*</sups><emph>p</emph> < .1, <sups>**</sups><emph>p</emph> < .05, <sups>***</sups><emph>p</emph> < .01.</item> </ulist> <hd id="AN0190550167-14">Testing the identifying assumptions</hd> <p>The regression discontinuity design assumes that assignment to either side of the threshold is as good as random. To check for any bunching just above or just below the threshold, we plot a density graph of the running variable (predicted poverty score) for the whole sample (Figure 2) and for each of the two subsamples (Figures A1 and A2 in the Appendix). A visual inspection of the density graphs suggests that bunching does not occur. More formally, we test for bunching by conducting McCrary's ([<reflink idref="bib31" id="ref35">31</reflink>]) density test using observations near the threshold. The log difference in height is 0.022 (s.e. 0.047) in the full sample, 0.019 (s.e. 0.060) in the sample of children exposed during early childhood, and 0.041 (s.e. 0.066) in the sample of children exposed while in utero.</p> <p> <img src="https://imageserver.ebscohost.com/img/embimages/rdk/JPA/01jan26/pam22663-fig-0002.jpg?ephost1=dGJyMNXb4kSepq84yOvqOLCmsE6epq5Srqa4SK6WxWXS" alt="pam22663-fig-0002.jpg" title="2 Density. [Colour figure can be viewed at wileyonlinelibrary.com]Notes: The figure shows the distribution in the range of −0.1 and 0.1 of the running variable. Each bar represents the fraction of households in specific values of the predicted poverty score. The vertical line corresponds to the eligibility cutoff." /> </p> <p></p> <p>To check whether covariates are balanced at baseline, we run equation (<reflink idref="bib1" id="ref36">1</reflink>) using a wide range of baseline household, mother, and child characteristics. Table 3 reports results from estimating the effect of the PANES program on various covariates at baseline. Most coefficients are small and not significantly different from zero, which aligns with the assumption that assignment around the threshold is as good as random. Moreover, a joint significance test yields a <emph>p</emph>‐value of 0.159. Most covariates have a strong correlation with the highest grade attained, yet they are balanced between treated and control groups (see column 5). Boys have lower educational attainment than girls; being born with low birth weight is negatively correlated with the highest grade attained; and children whose mothers have completed primary education attain higher grades than those with less‐educated mothers.</p> <p>3 TABLE Estimates of the effect of the PANES transfer on different covariates using baseline data and correlation of covariates with main outcome.</p> <p> <ephtml> <table><thead><tr><th /><th align="center">Non‐eligible mean</th><th align="center">Coefficient</th><th align="center">s.e.</th><th align="center"><italic>N</italic></th><th align="center">Correlation with outcome</th></tr><tr><th /><th align="center">(1)</th><th align="center">(2)</th><th align="center">(3)</th><th align="center">(4)</th><th align="center">(5)</th></tr></thead><tbody><tr><td>Child's indicators</td><td /><td /><td /><td /><td /></tr><tr><td>Child is a boy</td><td>0.510</td><td>0.008</td><td>(0.014)</td><td>19863</td><td>−0.191<ext-link /><sup>***</sup>(0.011)</td></tr><tr><td>Birth weight</td><td>3199</td><td>18.840</td><td>(22.140)</td><td>9362</td><td>0.000<ext-link /><sup>***</sup>(0.000)</td></tr><tr><td>Low birth weight</td><td>0.080</td><td>−0.007</td><td>(0.012)</td><td>9362</td><td>−0.180<ext-link /><sup>***</sup>(0.033)</td></tr><tr><td>Apgar score 1 minute<sup>†</sup></td><td>8.575</td><td>−0.037</td><td>(0.043)</td><td>9368</td><td>0.026<ext-link /><sup>***</sup>(0.009)</td></tr><tr><td>Apgar score 5 minutes<sup>†</sup></td><td>9.675</td><td>0.002</td><td>(0.031)</td><td>9366</td><td>0.044<ext-link /><sup>***</sup>(0.013)</td></tr><tr><td>Age in months in Dec 2007</td><td>31.099</td><td>−0.006</td><td>(0.008)</td><td>19863</td><td>0.029(0.019)</td></tr><tr><td>Mother's indicators</td><td /><td /><td /><td /><td /></tr><tr><td>Age</td><td>24.627</td><td>0.005</td><td>(0.278)</td><td>9290</td><td>−0.003<ext-link /><sup>***</sup>(0.001)</td></tr><tr><td>Complete primary education</td><td>0.925</td><td>0.014<ext-link /><sup>*</sup></td><td>(0.008)</td><td>19826</td><td>0.341<ext-link /><sup>***</sup>(0.020)</td></tr><tr><td>Complete secondary education</td><td>0.031</td><td>0.001</td><td>(0.005)</td><td>19826</td><td>0.130<ext-link /><sup>***</sup>(0.033)</td></tr><tr><td>Number of prenatal controls</td><td>7.463</td><td>0.218</td><td>(0.135)</td><td>9349</td><td>0.026<ext-link /><sup>***</sup>(0.003)</td></tr><tr><td>Gestational weeks</td><td>38.640</td><td>0.073</td><td>(0.077)</td><td>9169</td><td>0.026<ext-link /><sup>***</sup>(0.005)</td></tr><tr><td>Number of previous pregnancies</td><td>2.564</td><td>−0.219<ext-link /><sup>***</sup></td><td>(0.076)</td><td>9435</td><td>−0.046<ext-link /><sup>***</sup>(0.005)</td></tr><tr><td>Household's indicators</td><td /><td /><td /><td /><td /></tr><tr><td>Hot water</td><td>0.294</td><td>0.019</td><td>(0.012)</td><td>19859</td><td>0.081<ext-link /><sup>***</sup>(0.013)</td></tr><tr><td>Heater</td><td>0.192</td><td>0.001</td><td>(0.011)</td><td>19845</td><td>0.090<ext-link /><sup>***</sup>(0.014)</td></tr><tr><td>Kitchen</td><td>0.684</td><td>0.012</td><td>(0.014)</td><td>19862</td><td>0.113<ext-link /><sup>***</sup>(0.012)</td></tr><tr><td>Heating</td><td>0.007</td><td>−0.003</td><td>(0.002)</td><td>19833</td><td>−0.023(0.071)</td></tr><tr><td>Concrete floor</td><td>0.555</td><td>−0.012</td><td>(0.014)</td><td>19653</td><td>−0.050<ext-link /><sup>***</sup>(0.011)</td></tr><tr><td>Mud wall</td><td>0.920</td><td>0.010</td><td>(0.008)</td><td>19551</td><td>0.109<ext-link /><sup>***</sup>(0.019)</td></tr><tr><td>Block has electricity</td><td>0.978</td><td>0.000</td><td>(0.005)</td><td>19858</td><td>0.067*(0.035)</td></tr><tr><td>Block has piped water</td><td>0.940</td><td>0.010</td><td>(0.007)</td><td>19851</td><td>0.060<ext-link /><sup>***</sup>(0.023)</td></tr><tr><td>Block has sewage</td><td>0.409</td><td>0.050<ext-link /><sup>***</sup></td><td>(0.014)</td><td>19793</td><td>0.058<ext-link /><sup>***</sup>(0.011)</td></tr><tr><td>Block has trash collection</td><td>0.900</td><td>0.017<ext-link /><sup>*</sup></td><td>(0.009)</td><td>19835</td><td>0.092<ext-link /><sup>***</sup>(0.018)</td></tr><tr><td>Block has paved streets</td><td>0.666</td><td>0.006</td><td>(0.014)</td><td>19797</td><td>0.032<ext-link /><sup>***</sup>(0.012)</td></tr><tr><td>Block has sidewalk</td><td>0.701</td><td>0.009</td><td>(0.013)</td><td>19808</td><td>0.077<ext-link /><sup>***</sup>(0.012)</td></tr><tr><td>House</td><td>0.879</td><td>−0.015</td><td>(0.010)</td><td>19533</td><td>0.068<ext-link /><sup>***</sup>(0.016)</td></tr><tr><td>Microwave</td><td>0.045</td><td>0.002</td><td>(0.005)</td><td>19863</td><td>0.111<ext-link /><sup>***</sup>(0.029)</td></tr><tr><td>Refrigerator</td><td>0.662</td><td>0.018</td><td>(0.014)</td><td>19848</td><td>0.065<ext-link /><sup>***</sup>(0.011)</td></tr><tr><td>Freezer</td><td>0.092</td><td>0.008</td><td>(0.008)</td><td>19824</td><td>0.035<ext-link /><sup>*</sup>(0.020)</td></tr><tr><td>Washing machine</td><td>0.186</td><td>0.000</td><td>(0.011)</td><td>19863</td><td>0.021(0.015)</td></tr><tr><td>Dishwasher</td><td>0.002</td><td>0.001</td><td>(0.001)</td><td>19849</td><td>0.065(0.128)</td></tr><tr><td>TV</td><td>0.791</td><td>0.005</td><td>(0.012)</td><td>19859</td><td>0.104<ext-link /><sup>***</sup>(0.013)</td></tr><tr><td>VCR</td><td>0.040</td><td>0.008</td><td>(0.005)</td><td>19857</td><td>−0.018(0.030)</td></tr><tr><td>Cable TV</td><td>0.134</td><td>0.010</td><td>(0.009)</td><td>19863</td><td>0.122<ext-link /><sup>***</sup>(0.018)</td></tr><tr><td>Computer</td><td>0.010</td><td>0.001</td><td>(0.003)</td><td>19855</td><td>0.143**(0.063)</td></tr><tr><td>Car</td><td>0.031</td><td>0.003</td><td>(0.005)</td><td>19863</td><td>0.080**(0.035)</td></tr><tr><td>Home owned</td><td>0.498</td><td>−0.006</td><td>(0.014)</td><td>19831</td><td>−0.041<ext-link /><sup>***</sup>(0.011)</td></tr><tr><td>Number of rooms</td><td>2.407</td><td>0.059</td><td>(0.055)</td><td>19861</td><td>0.016<ext-link /><sup>***</sup>(0.003)</td></tr><tr><td>Number of bedrooms</td><td>1.721</td><td>0.047<ext-link /><sup>**</sup></td><td>(0.024)</td><td>19861</td><td>0.022<ext-link /><sup>***</sup>(0.007)</td></tr><tr><td>Receipt of Plan de Equidad</td><td>0.804</td><td>−0.006</td><td>(0.011)</td><td>19392</td><td>0.065<ext-link /><sup>***</sup>(0.014)</td></tr></tbody></table> </ephtml> </p> <ulist> <item>5 <emph>Notes</emph>: In column 2 we report estimates of equation (<reflink idref="bib1" id="ref37">1</reflink>) using different covariates at baseline as outcome variables. We use pre‐program data for those covariates that are not measured at baseline: birth weight, low birth weight, Apgar 1 minute, Apgar 5 minutes, age of the mother at birth, number of prenatal controls, gestational weeks and number of previous pregnancies. Estimates are obtained using a bandwidth of 0.075 around the threshold and a first order polynomial. In column 5 we report the correlation of each covariate with the outcome highest grade attained. We obtain these correlations by regressing highest grade attained on each covariate and conditioning on month times year of birth fixed effects, and month times year of baseline visit fixed effects. Standard errors (s.e.) are reported in parentheses. <emph>N</emph> corresponds to number of observations. <sups>†</sups> The Apgar score is a widely accepted method for assessing a newborn's condition right after birth and gauging the effectiveness of any resuscitation efforts, maintaining its status as the benchmark for neonatal evaluation. It is assessed at two different times after birth: at 1 minute and at 5 minutes. In summary, the 1‐minute Apgar score focuses on the neonate's immediate response to birth, while the 5‐minute score assesses how the baby is adapting to life outside the womb and the effectiveness of any resuscitative efforts. Higher values represent better health conditions.</item> <item>6 * <emph>p</emph> < .1, ** <emph>p</emph> < .05, *** <emph>p</emph> < .01.</item> </ulist> <p>We include estimates of the effect of the PANES transfer on different covariates for children exposed to the program during early childhood and for children exposed to the program while in utero separately in Tables A5 and A6 in the Appendix. Balancing in the sample of children exposed while in utero is similar to that in the full sample, with only three coefficients showing significance. This is consistent with the identification assumption that assignment around the threshold is as good as random. In the sample of children exposed to PANES during early childhood, coefficients are significant in a few more cases, but the signs of these coefficients go in the opposite direction of the correlation of the covariate with the outcome "highest grade attained." In any case, we control for all pre‐treatment covariates.</p> <hd id="AN0190550167-16">EMPIRICAL RESULTS</hd> <p></p> <hd id="AN0190550167-17">Main results</hd> <p>In Table 4, we report estimates of the effect of receiving the PANES transfer during early childhood and while in utero on educational attainment 8 to 12 years later. In Panel A, we report estimates for the whole sample; in Panel B, we report estimates for children exposed during early childhood; and in Panel C, we report estimates for those exposed while in utero. For each outcome, we use two specifications: one with controls and one without controls. Overall, coefficients go in the expected direction: the effects on the highest grade attained are positive, the effects on educational delay are negative, and the effects on dropout rates are negative. For the entire sample (Panel A), there is a negative and significant effect on the probability of being delayed (the <emph>p</emph>‐value is 0.07 and 0.08 in columns 3 and 4, respectively). The sharpened <emph>q</emph>‐values cross the 10% threshold. When splitting the sample, we find that eligible children who were exposed to the program during early childhood (Panel B) have higher educational attainment (the <emph>p</emph>‐value in columns 1 and 2 is 0.08). Additionally, we find that the effect on educational attainment is due to a lower incidence of educational delay (the <emph>p</emph>‐value is 0.06 and 0.08 in columns 3 and 4, respectively). These effects are robust when accounting for multiple hypotheses testing using sharpened <emph>q</emph>‐values. We find no significant effects on dropout rates. This is unsurprising, given that we are considering children primarily in primary school, where dropout is less likely than in secondary school. Educational attainment of children exposed to the program while in utero (Panel C) is not significantly different between eligible and ineligible households for any of the outcomes considered.</p> <p>4 TABLE Effect of receiving the PANES transfer on educational attainment.</p> <p> <ephtml> <table><thead><tr><th /><th align="center">Highest grade attained</th><th align="center">Delay</th><th align="center">Dropout</th></tr><tr><th /><th align="center">(1)</th><th align="center">(2)</th><th align="center">(3)</th><th align="center">(4)</th><th align="center">(5)</th><th align="center">(6)</th></tr></thead><tbody><tr><td>Panel A: All observations</td><td /><td /><td /><td /><td /><td /></tr><tr><td>Coefficient</td><td>0.043</td><td>0.047</td><td>−0.040<ext-link /><sup>*</sup></td><td>−0.038<ext-link /><sup>*</sup></td><td>−0.001</td><td>−0.002</td></tr><tr><td>s.e.</td><td>(0.044)</td><td>(0.040)</td><td>(0.022)</td><td>(0.022)</td><td>(0.007)</td><td>(0.007)</td></tr><tr><td>q‐value</td><td /><td /><td>[0.192]</td><td>[0.185]</td><td /><td /></tr><tr><td>Observations</td><td align="center">11613</td><td align="center">13586</td><td align="center">16597</td><td align="center">16744</td><td align="center">18224</td><td align="center">18297</td></tr><tr><td>CCT bandwidth</td><td>0.045</td><td>0.051</td><td>0.062</td><td>0.063</td><td>0.068</td><td>0.068</td></tr><tr><td>Panel B: Exposed during early‐childhood</td><td /><td /><td /><td /><td /><td /></tr><tr><td>Coefficient</td><td>0.125<ext-link /><sup>*</sup></td><td>0.112<ext-link /><sup>*</sup></td><td>−0.069<ext-link /><sup>*</sup></td><td>−0.064<ext-link /><sup>*</sup></td><td>0.008</td><td>0.007</td></tr><tr><td>s.e.</td><td>(0.071)</td><td>(0.065)</td><td>(0.036)</td><td>(0.037)</td><td>(0.011)</td><td>(0.010)</td></tr><tr><td>q‐value</td><td>[0.083]</td><td>[0.092]</td><td>[0.083]</td><td>[0.092]</td><td /><td /></tr><tr><td>Observations</td><td align="center">6553</td><td align="center">7376</td><td align="center">7608</td><td align="center">7264</td><td align="center">8350</td><td align="center">9111</td></tr><tr><td>CCT bandwidth</td><td>0.052</td><td>0.058</td><td>0.060</td><td>0.057</td><td>0.066</td><td>0.072</td></tr><tr><td>Panel C: Exposed while in‐utero</td><td /><td /><td /><td /><td /><td /></tr><tr><td>Coefficient</td><td>−0.001</td><td>−0.002</td><td>−0.015</td><td>−0.012</td><td>−0.009</td><td>−0.009</td></tr><tr><td>s.e.</td><td>(0.034)</td><td>(0.034)</td><td>(0.024)</td><td>(0.023)</td><td>(0.008)</td><td>(0.008)</td></tr><tr><td>Observations</td><td align="center">11917</td><td align="center">11809</td><td align="center">12065</td><td align="center">12453</td><td align="center">11973</td><td align="center">11667</td></tr><tr><td>CCT bandwidth</td><td>0.087</td><td>0.086</td><td>0.088</td><td>0.092</td><td>0.088</td><td>0.084</td></tr><tr><td>Controls</td><td align="center">No</td><td align="center">Yes</td><td align="center">No</td><td align="center">Yes</td><td align="center">No</td><td align="center">Yes</td></tr></tbody></table> </ephtml> </p> <ulist> <item>7 <emph>Notes</emph>: Each cell corresponds to a different regression. In Panel A we use the sample of children whose family received the PANES transfer during early childhood. In Panel B we use the sample of children whose family received the PANES transfer while the child was in utero. In Panel C we use all observations. We estimate equation (<reflink idref="bib1" id="ref38">1</reflink>) using different outcome variables. In columns 1 and 2 we report results using as outcome variable highest grade attained in education. In columns 3 and 4 we report results using as outcome variable an indicator for delay in educational attainment that takes value 1 if the child is enrolled at a lower grade than the one determined by her year and month of birth and a regular track. In columns 5 and 6 we report results using as outcome variable an indicator for whether the child dropped out from education, where dropout is measured as being two or more years not enrolled in any program. We report the estimates obtained when using the CCT bandwidth and polynomial defined according to Calonico et al. ([<reflink idref="bib19" id="ref39">19</reflink>]). Sharpened <emph>q</emph>‐values are reported in squared brackets only for significant coefficients. CCT bandwidths are reported below each coefficient and CCT polynomial is 1 in all cases. All estimations include month times year of birth fixed effects, and month times year of baseline visit fixed effects. In even columns we present results of estimating equation (<reflink idref="bib1" id="ref40">1</reflink>) using the following additional controls: gender of the child, an indicator for whether the mother completed primary school, number of bedrooms in the household and indicators for whether the household's block has sewage and trash collection. All controls are included as indicator variables and include a category for missing observations. Standard errors (s.e.) are reported in parentheses and number of observations are reported below each coefficient.</item> <item>8 * <emph>p</emph> < .1, ** <emph>p</emph> < .05, *** <emph>p</emph> < .01.</item> </ulist> <hd id="AN0190550167-18">Heterogeneous effects by low birth weight</hd> <p>Children who were first exposed to PANES during early childhood were born at the time of a severe economic crisis. In this subsection, we explore whether transfers have a stronger effect on education for children born with a higher risk of weighing less than 2500 grams. Table 5 shows heterogeneous effects of receiving the PANES transfer on education by low birth weight. Estimations only consider observations of children born in the pre‐program period, and thus, who were exposed to the program during early childhood. The first two columns correspond to children born with low birth weight (defined as weighing less than 2500 grams), and the last two columns correspond to children born with normal birth weight. Barely eligible children born with a weight less than 2500 grams have higher educational attainment and a lower incidence of delay compared to barely ineligible children born with the same condition. Despite having 800 observations, the effect is significant at least at the 5% level, indicating that its magnitude is especially large. The effect is also significant when considering sharpened <emph>q</emph>‐values. There is also an effect on dropout, but it goes in the opposite direction than expected. In particular, the likelihood of dropout is higher among barely eligible children born with low birth weight compared to barely ineligible children born with low birth weight. This effect is significant at the 10% level when considering unadjusted <emph>p</emph>‐values, but becomes non‐significant or barely significant when considering sharpened <emph>q</emph>‐values in the specifications without and with controls, respectively. Overall, the findings from this analysis suggest that the program had stronger effects on children born when the economic context was more unfavorable and with a higher risk of low birth weight.</p> <p>5 TABLE Heterogeneous effects of receiving the PANES transfer on education by low birth weight.</p> <p> <ephtml> <table><thead><tr><th /><th align="center">Born with low birth weight</th><th align="center">Born with normal birth weight</th></tr><tr><th /><th align="center">(1)</th><th align="center">(2)</th><th align="center">(3)</th><th align="center">(4)</th></tr></thead><tbody><tr><td>Panel A: Highest grade attained</td><td /><td /><td /><td /></tr><tr><td>Coefficient</td><td>0.500<ext-link /><sup>**</sup></td><td>0.529<ext-link /><sup>***</sup></td><td>0.078</td><td>0.070</td></tr><tr><td>s.e.</td><td>(0.199)</td><td>(0.198)</td><td>(0.067)</td><td>(0.058)</td></tr><tr><td>q‐values</td><td>[0.016]</td><td>[0.010]</td><td /><td /></tr><tr><td>Observations</td><td align="center">783</td><td align="center">761</td><td align="center">6936</td><td align="center">8434</td></tr><tr><td>CCT bandwidth</td><td>0.075</td><td>0.072</td><td>0.060</td><td>0.074</td></tr><tr><td>Panel B: Delay</td><td /><td /><td /><td /></tr><tr><td>Coefficient</td><td>−0.241<ext-link /><sup>**</sup></td><td>−0.255<ext-link /><sup>***</sup></td><td>−0.050</td><td>−0.040</td></tr><tr><td>s.e.</td><td>(0.099)</td><td>(0.099)</td><td>(0.035)</td><td>(0.035)</td></tr><tr><td>q‐values</td><td>[0.016]</td><td>[0.010]</td><td /><td /></tr><tr><td>Observations</td><td align="center">865</td><td align="center">848</td><td align="center">7923</td><td align="center">7657</td></tr><tr><td>CCT bandwidth</td><td>0.084</td><td>0.082</td><td>0.068</td><td>0.067</td></tr><tr><td>Panel C: Dropout</td><td /><td /><td /><td /></tr><tr><td>Coefficient</td><td>0.065<ext-link /><sup>*</sup></td><td>0.069<ext-link /><sup>*</sup></td><td>0.004</td><td>0.003</td></tr><tr><td>s.e.</td><td>(0.039)</td><td>(0.041)</td><td>(0.011)</td><td>(0.010)</td></tr><tr><td>q‐values</td><td>[0.108]</td><td>[0.098]</td><td /><td /></tr><tr><td>Observations</td><td align="center">844</td><td align="center">789</td><td align="center">8591</td><td align="center">9259</td></tr><tr><td>CCT bandwidth</td><td>0.081</td><td>0.076</td><td>0.075</td><td>0.082</td></tr><tr><td>Controls</td><td align="center">No</td><td align="center">Yes</td><td align="center">No</td><td align="center">Yes</td></tr></tbody></table> </ephtml> </p> <ulist> <item>9 <emph>Notes</emph>: Each cell corresponds to a different regression. Estimations consider the sample of children whose family received the PANES transfer during early‐childhood. We estimate equation (<reflink idref="bib1" id="ref41">1</reflink>) using different outcome variables and for two different subsamples. Each panel corresponds to a different outcome. In columns 1 and 2 we report results for children with low birth weight. In columns 3 and 4 we report results for children without low birth weight. We report the estimates obtained when using the CCT bandwidth and polynomial defined according to Calonico et al. ([<reflink idref="bib19" id="ref42">19</reflink>]). Sharpened <emph>q</emph>‐values are reported in squared brackets only for significant coefficients. CCT bandwidths are reported below each coefficient and CCT polynomial is 1 in all cases. All estimations include month times year of birth fixed effects, and month times year of baseline visit fixed effects. In even columns we present results of estimating equation (<reflink idref="bib1" id="ref43">1</reflink>) using the following additional controls: gender of the child, an indicator for whether the mother completed primary school, number of bedrooms in the household and indicators for whether the household's block has sewage and trash collection. All controls are included as indicator variables and include a category for missing observations. Standard errors (s.e.) are reported in parentheses and number of observations are reported below each coefficient.</item> <item>10 * <emph>p</emph> < .1, ** <emph>p</emph> < .05, *** <emph>p</emph> < .01.</item> </ulist> <hd id="AN0190550167-19">Exploring short run impacts of PANES on low birth weight</hd> <p>We found no evidence supporting the idea that the PANES program improved educational attainment for those exposed while in utero. Given the extensive literature on the effects of low birth weight on educational attainment (Figlio et al., [<reflink idref="bib22" id="ref44">22</reflink>]) and previous evidence showing that PANES improved health at birth, in this subsection we explore whether low birth weight is a potential mechanism behind long‐term educational outcomes.</p> <p>We use a regression discontinuity approach and compare health at birth outcomes between eligible and ineligible children who were born during the program period. Table A10 in the Appendix shows that the subsample of low birth weight children is balanced. A visual inspection of the incidence of low birth weight on both sides of the PANES eligibility cutoff (Figure 3) suggests that the program had no impact on health at birth. Table 6 shows results from estimating equation (<reflink idref="bib1" id="ref45">1</reflink>) using low birth weight as the outcome variable. We find that the relevant coefficients are negative, but they are small in magnitude and not significant.</p> <p> <img src="https://imageserver.ebscohost.com/img/embimages/rdk/JPA/01jan26/pam22663-fig-0003.jpg?ephost1=dGJyMNXb4kSepq84yOvqOLCmsE6epq5Srqa4SK6WxWXS" alt="pam22663-fig-0003.jpg" title="3 Low birth weight around the PANES cutoff. [Colour figure can be viewed at wileyonlinelibrary.com]Notes: The vertical line corresponds to the eligibility cutoff, above which households are eligible to the program and below which they are not eligible to the program. There are 10 bins at each side of the cutoff and the range is −0.1, 0.1. Each dot represents the average low birth weight in that bin. The two solid lines represent the best fit from a linear regression from each side of the cut‐off." /> </p> <p></p> <p>6 TABLE 2SLS estimates of the effect of the PANES transfer on low birth weight (<2.500 kg) children born during program period.</p> <p> <ephtml> <table><thead><tr><th /><th align="center">(1)</th><th align="center">(2)</th><th align="center">(3)</th><th align="center">(4)</th><th align="center">(5)</th><th align="center">(6)</th><th align="center">(7)</th></tr></thead><tbody><tr><td>1. No controls</td><td>−0.001</td><td>−0.006</td><td>0.000</td><td>−0.008</td><td>−0.009</td><td>−0.008</td><td>−0.003</td></tr><tr><td /><td>(0.012)</td><td>(0.019)</td><td>(0.014)</td><td>(0.027)</td><td>(0.018)</td><td>(0.027)</td><td>(0.013)</td></tr><tr><td>Observations</td><td align="center">13283</td><td align="center">13283</td><td align="center">10309</td><td align="center">6905</td><td align="center">6905</td><td align="center">6905</td><td align="center">14243</td></tr><tr><td>Bandwidth</td><td>0.1</td><td>0.1</td><td>0.075</td><td>0.075</td><td>0.05</td><td>0.05</td><td>0.114</td></tr><tr><td>Order of polynomial</td><td align="center">1</td><td align="center">2</td><td align="center">1</td><td align="center">2</td><td align="center">1</td><td align="center">2</td><td align="center">1</td></tr><tr><td>2. Controls</td><td>−0.001</td><td>−0.005</td><td>0.001</td><td>−0.006</td><td>−0.009</td><td>−0.006</td><td>−0.003</td></tr><tr><td /><td>(0.012)</td><td>(0.019)</td><td>(0.014)</td><td>(0.027)</td><td>(0.018)</td><td>(0.027)</td><td>(0.013)</td></tr><tr><td>Observations</td><td align="center">13283</td><td align="center">13283</td><td align="center">10309</td><td align="center">6905</td><td align="center">6905</td><td align="center">6905</td><td align="center">13384</td></tr><tr><td>Bandwidth</td><td>0.1</td><td>0.1</td><td>0.075</td><td>0.075</td><td>0.05</td><td>0.05</td><td>0.101</td></tr><tr><td>Order of polynomial</td><td align="center">1</td><td align="center">2</td><td align="center">1</td><td align="center">2</td><td align="center">1</td><td align="center">2</td><td align="center">1</td></tr></tbody></table> </ephtml> </p> <ulist> <item>11 <emph>Notes</emph>: Each cell corresponds to a different regression. Sample includes children that were born during the program period. In columns 1 through 6 we estimate equation (<reflink idref="bib1" id="ref46">1</reflink>) for three different bandwidths around the eligibility threshold and two different orders of polynomial. In column 7 we report the estimates obtained when using the bandwidth and polynomial defined according to Calonico et al. ([<reflink idref="bib19" id="ref47">19</reflink>]). All estimations include month times year of birth fixed effects, and month times year of baseline visit fixed effects. Row 1 presents regressions with no additional controls while row 2 reports results with the following additional controls: gender of the child, an indicator for whether the mother completed primary school, number of bedrooms in the household and indicators for whether the household's block has sewage and trash collection. Controls are included as indicator variables and include a category for missing observations. Standard errors are reported in parentheses and number of observations are reported below each coefficient.</item> <item>12 * * <emph>p</emph> < .1, ** <emph>p</emph> < .05, *** <emph>p</emph> < .01.</item> </ulist> <p>Our findings align with Buser et al. ([<reflink idref="bib18" id="ref48">18</reflink>]), who found no effect on weight and height from receiving a cash transfer in Ecuador. Our conclusion is that low birth weight cannot be considered a first‐stage effect for our long‐term impacts on education for children exposed to the program while in utero.</p> <p>Following Amarante et al. ([<reflink idref="bib5" id="ref49">5</reflink>]), we also report results on health at birth using a localized difference‐in‐differences estimator (see Appendix B for details of this identification strategy). Table 7 reports results from estimating equation (<reflink idref="bib2" id="ref50">2</reflink>) using low birth weight as the outcome variable (see Appendix B). From our estimations, we cannot reject the null hypothesis of no effect of the PANES transfer on the incidence of low birth weight. The estimated coefficients are negative and mostly non‐significant. Standard errors increase as we get closer to the cutoff. These results differ from the findings of Amarante et al. ([<reflink idref="bib5" id="ref51">5</reflink>]), and we attribute this to the fact that our sample is different. Specifically, our database does not include multiple births, which on average are those born with lower weights. In any case, as we discuss further in Appendix B, we cannot validate all of the assumptions of the localized difference‐in‐differences in the setting of this paper. Therefore, our regression discontinuity estimates are our preferred specification.</p> <p>7 TABLE 2SLS estimates of the effect of the PANES transfer on low birth weight (<2.500 kg) using a difference in discontinuity design.</p> <p> <ephtml> <table><thead><tr><th /><th align="center">(1)</th><th align="center">(2)</th><th align="center">(3)</th><th align="center">(4)</th><th align="center">(5)</th><th align="center">(6)</th></tr></thead><tbody><tr><td>1. No controls</td><td>−0.011<ext-link /><sup>*</sup></td><td>−0.011<ext-link /><sup>*</sup></td><td>−0.013</td><td>−0.013</td><td>−0.014</td><td>−0.014</td></tr><tr><td /><td>(0.006)</td><td>(0.006)</td><td>(0.008)</td><td>(0.008)</td><td>(0.010)</td><td>(0.010)</td></tr><tr><td>Observations</td><td align="center">56856</td><td align="center">56856</td><td align="center">25384</td><td align="center">25384</td><td align="center">19670</td><td align="center">19670</td></tr><tr><td>2. Controls</td><td>−0.013<ext-link /><sup>**</sup></td><td>−0.013<ext-link /><sup>**</sup></td><td>−0.013</td><td>−0.013</td><td>−0.013</td><td>−0.013</td></tr><tr><td /><td>(0.006)</td><td>(0.006)</td><td>(0.008)</td><td>(0.008)</td><td>(0.010)</td><td>(0.010)</td></tr><tr><td>Observations</td><td align="center">56856</td><td align="center">56856</td><td align="center">25384</td><td align="center">25384</td><td align="center">19670</td><td align="center">19670</td></tr><tr><td>Range</td><td align="center">All</td><td align="center">All</td><td>0.1</td><td>0.1</td><td>0.075</td><td>0.075</td></tr><tr><td>Order of polynomial</td><td align="center">1</td><td align="center">2</td><td align="center">1</td><td align="center">2</td><td align="center">1</td><td align="center">2</td></tr></tbody></table> </ephtml> </p> <ulist> <item>13 <emph>Notes</emph>: Each cell corresponds to a different regression. Sample contains pooled preprogram and program period data, corresponding to children born between the years 2003 and 2007. In columns 1 through 6 we estimate equation (<reflink idref="bib2" id="ref52">2</reflink>) for three different ranges around the eligibility threshold and three different orders of polynomial. All estimations include month times year of birth fixed effects, and month times year of baseline visit fixed effects. Row 1 presents regressions with no additional controls while row 2 reports results with the following additional controls: gender of the child, number of previous pregnancies of the mother, an indicator for whether the mother completed primary school, indicators for geographic department of the household at baseline, for whether the household has centralized hot water, heater, kitchen, microwave, refrigerator, freezer, washing machine, dishwasher, TV, VCR, cable TV, computer, car; whether the block has electricity, piped water, sewage, trash collection, paved streets, sidewalk; whether the home is a house, is owned, and indicators for material of the floor and walls. Controls are included as indicator variables and include a category for missing observations. Standard errors are reported in parentheses and number of observations are reported below each coefficient.</item> <item>14 * <emph>p</emph> < .1, ** <emph>p</emph> < .05, *** <emph>p</emph> < .01.</item> </ulist> <hd id="AN0190550167-21">DISCUSSION</hd> <p>In this paper, we explore whether expanding economic resources during early life, in the form of an unconditional cash transfer, improves later outcomes. Specifically, we examine the effect of being exposed to the Uruguayan PANES during the prenatal period and early childhood on educational outcomes 8 to 12 years later. We use a rich dataset that matches administrative data from three sources, allowing us to distinguish effects for children who were exposed since they were in their mother's womb and children who were exposed to the program in their first years of life.</p> <p>Our results show that children from eligible households that started receiving the program after they were born exhibit mild improvements in educational attainment and a reduction in the likelihood of educational delay. These results are significant at the 10% level. We find an increase in educational attainment of 0.1 years of education and a decrease in the likelihood of delay by 6.9 percentage points around the eligibility cutoff. These results correspond to local average treatment effects around the cutoff point. Considering that the amount of the transfer represented almost half of the average household income among the target population, the magnitude of the effects of PANES on education is relatively small.</p> <p>One potential explanation for why we find results for the subsample of relatively older children but not for the relatively younger children is that the former were born and started receiving the program when the Uruguayan context was more unfavorable and poverty rates were higher. Note that total income in PANES applicant families doubled between the pre‐program and program periods. Our interpretation is that, rather than arguing against Heckman's theory of dynamic complementarities, our findings suggest that the program impacts children born in families close to the eligibility cutoff when children are born in a worse economic situation and with a higher risk of low birth weight.</p> <p>Another possible explanation for the lack of effects for the group exposed while in utero is that older cohorts are observed for more years in the education system, allowing a higher margin of response. This is specifically relevant for dropout rates, given that in Uruguay these begin to rise significantly during ages 12 to 14. By the conclusion of this stage, a significant percentage of students, particularly from lower socioeconomic backgrounds, disengage from the education system. In future research, we plan to incorporate more years of education data to observe all students through the end of secondary school, where dropout rates reach 40% to 50%.</p> <p>While we are considering a cash transfer in the Latin American context, our results align with studies on the longer‐term effects of unconditional cash transfers in Africa (Blattman et al., [<reflink idref="bib17" id="ref53">17</reflink>]; Haushofer & Shapiro, [<reflink idref="bib27" id="ref54">27</reflink>]). However, the evidence in this paper contrasts with findings from other Latin American countries regarding the effect of conditional cash transfers on educational attainment in the longer run (Millán et al., [<reflink idref="bib32" id="ref55">32</reflink>]).</p> <hd id="AN0190550167-22">DATA AVAILABILITY STATEMENT</hd> <p>The data that support the findings of this study are available from the Ministry of Social Development of Uruguay. Restrictions apply to the availability of these data, which were used under license for this study. Data are available from the authors with the permission of the Ministry of Social Development.</p> <p>GRAPH: Appendix Tables and Figures</p> <ref id="AN0190550167-23"> <title> Footnotes </title> <blist> <bibl id="bib1" idref="ref29" type="bt">1</bibl> <bibtext> The authors find that the PANES program led to a drop in the incidence of low birth weight that ranges between 19% and 25% and that fertility was not affected by program participation. The result could be considered a "first stage" effect for our long‐term educational outcomes, although the program may affect long‐term outcomes also through other mechanisms (Almond et al., [2]).</bibtext> </blist> <blist> <bibl id="bib2" idref="ref1" type="bt">2</bibl> <bibtext> Birth weight has emerged as the main focus of health policy, both in the United States and elsewhere, and has been used to evaluate the effectiveness of social policy (Almond et al., [1]). Research has shown that birth weight can affect neonatal outcomes and long‐run health outcomes (Black et al., [16]; Oreopoulos et al., [33]), and even the birth weight of the next generation (Black et al., [16]; Royer, [37]). Birth weight can also affect non‐health outcomes such as schooling, wages, IQ, and test scores (Behrman & Rosenzweig, [13]; Black et al., [16]; Oreopoulos et al., [33]; Rosenzweig & Zhang, [36]; Royer, [37]; Torche & Echevarría, [38]).</bibtext> </blist> <blist> <bibl id="bib3" idref="ref26" type="bt">3</bibl> <bibtext> Amarante et al. ([5]) used a localized difference‐in‐differences strategy while we use a regression discontinuity design. When Amarante et al. ([5]) used a regression discontinuity design, they did not find significant impacts of PANES on low birth weight. When we perform a localized difference‐in‐differences strategy, we do not find robust results showing that the program improved health at birth. We discuss this issue further in the section "Exploring Short‐Run Impacts of PANES on Low Birth Weight."</bibtext> </blist> <blist> <bibl id="bib4" idref="ref18" type="bt">4</bibl> <bibtext> Benhassine et al. ([14]) showed that transfers can serve as an effective policy tool to promote education if they are labeled as explicitly intended to be used for educational purposes. Labeled cash transfers are a middle ground between unconditional cash transfers and conditional cash transfers, leveraging the power of labeling to influence behavior without imposing rigid requirements.</bibtext> </blist> <blist> <bibl id="bib5" idref="ref4" type="bt">5</bibl> <bibtext> For example, a recent study for Nicaragua shows that cash transfers to families with children aged 7 to 13 led to higher market participation and earnings (for men) 10 years after its implementation (Barham et al., [11]).</bibtext> </blist> <blist> <bibl id="bib6" idref="ref19" type="bt">6</bibl> <bibtext> In 2003, Uruguay had a population of around 3.3 million people, and per capita GDP was about 8,000 USD. The country offers free public education from elementary school to university. There are 14 years of mandatory schooling: 2 in elementary school, 6 in primary school, and 6 in secondary school. While primary education is universal, secondary school completion rates pose a significant challenge for the Uruguayan government.</bibtext> </blist> <blist> <bibl id="bib7" type="bt">7</bibl> <bibtext> One of the variables used to predict the poverty score was the household's value in a wealth index. The variables included in the latter measure are listed in Appendix Table A2. All appendices are available at the end of this article as it appears in JPAM online. Go to the publisher's website and use the search engine to locate the article at <ulink href="http://onlinelibrary.wiley.com">http://onlinelibrary.wiley.com</ulink>.</bibtext> </blist> <blist> <bibl id="bib8" idref="ref24" type="bt">8</bibl> <bibtext> This figure was calculated using the Uruguayan Continuous Household Survey of 2004. Similar results are obtained when using the 2005 wave. Income is substantially lower outside Montevideo, the capital city of Uruguay, which explains why 70% of applicants live outside the capital city. The fixed amount of $1,360 Uruguayan pesos represents slightly more than 50% of monthly average household income among the poorest 10% of households that do not live in Montevideo and slightly less than 40% of monthly average household income among the poorest 10% of households that live in Montevideo. With respect to the whole income distribution of the country, the transfer represents 9% of monthly household average income.</bibtext> </blist> <blist> <bibl id="bib9" idref="ref9" type="bt">9</bibl> <bibtext> Our calculations are in line with Amarante and Vigorito ([7]) and Amarante et al. ([6]), who stated that the monthly amount of the transfer corresponded to half (50%) of the pre‐program household selfreported income. In Amarante et al. ([5]), the authors stated that the amount of the transfer represented a quarter of self‐reported income (25%).</bibtext> </blist> <blist> <bibtext> Households that became ineligible before the end of the program are still considered part of the treatment group.</bibtext> </blist> <blist> <bibtext> This does not necessarily mean that all households in the analysis received social benefits by definition. Almost all PANES applicants were visited by MIDES at another point in time due to other program applications.</bibtext> </blist> <blist> <bibtext> Within the program period, multiple births were equally likely for PANES recipients as for controls, easing concerns of selection bias. Infants born in multiple births have, on average, lower birth weights than those born in single‐order births, so our results may be sensitive to the inclusion of twins, triplets, and higher‐order births.</bibtext> </blist> <blist> <bibtext> We acknowledge that we do not measure completed education and that highest grade attained is a truncated variable. We have performed our estimations using an alternative outcome variable that measures the likelihood of enrolling in seventh grade (first year of secondary school) with no delay which excludes the possibility of truncation for younger students. Children that had not reach Grade 7 in 2017 were excluded from the estimation. The results are qualitatively equivalent to the ones we show in our main tables (see Appendix Table A7).</bibtext> </blist> <blist> <bibtext> In Uruguay, the requirement to enter the public education system is to have the age corresponding to the level before April 30 of the school year. That causes most children (2/3) to reach the age corresponding to the level during the school year and that 1/3 of the children do so the following year.</bibtext> </blist> <blist> <bibtext> One observation per child is used and we assess all children at a common reference point: the year 2017. For example, one observation corresponds to a child born in 2007 who attained 5 years of education in 2017, and another observation corresponds to a child born in 2003 who attained 9 years of education in 2017.</bibtext> </blist> <blist> <bibtext> A third explanation could be that the parents delayed the child's initial enrollment in the first grade of education. We are not able to capture this as a separate outcome because we do not observe the full educational trajectory of the child and therefore do not know in which year they entered school. In our setting, having parents who enroll children in a higher cohort than they should is unlikely to be problematic in terms of our outcome measures because if these kids repeat a grade we would still consider them as nondelayed. Even though age cutoffs to enter preschool are not strictly enforced in Uruguay, the children who enroll early are a minority, and it is more common to see children enrolled late instead.</bibtext> </blist> <blist> <bibtext> We are not assessing the balancing properties of the sample in this table. We do so in Table 3 further in the text.</bibtext> </blist> <blist> <bibtext> The month‐times‐year‐of‐birth fixed effects control for shocks affecting both treated and control groups. Cohort and age effects cannot be disentangled since we observe data at a fixed point in time, and all children of the same age belong to the same cohort. The month‐times‐year‐of‐baseline‐visit fixed effects control for common shocks affecting households when constructing the poverty score.</bibtext> </blist> <blist> <bibtext> We control for covariates that were not used to predict the eligibility score (see Appendix Tables A1 and A2), except for those that are unbalanced at baseline. Specifically, we control for the child's gender, the mother's educational level, and indicators for whether the household's block has sewage and trash collection, as well as the number of bedrooms in the household.</bibtext> </blist> <blist> <bibtext> Calonico et al. ([19]) incorporated the latest advances in regression discontinuity methods and refined the estimator proposed by Imbens and Kalyanaraman ([28]).</bibtext> </blist> <blist> <bibtext> Note that the normalized predicted poverty score ranges from <ephtml> <math display="inline" altimg="urn:x-wiley:02768739:media:pam22663:pam22663-math-0002" xmlns="http://www.w3.org/1998/Math/MathML"><semantics><mo>−</mo><annotation encoding="application/x-tex">$ - $</annotation></semantics></math> </ephtml> 0.19 to 0.95 in our sample.</bibtext> </blist> <blist> <bibtext> We obtain very similar results when using a second‐order polynomial function (see Table A4 in the Appendix).</bibtext> </blist> <blist> <bibtext> We use observations that have a value of the running variable in the range <ephtml> <math display="inline" altimg="urn:x-wiley:02768739:media:pam22663:pam22663-math-0003" xmlns="http://www.w3.org/1998/Math/MathML"><semantics><mo>−</mo><annotation encoding="application/x-tex">$ - $</annotation></semantics></math> </ephtml> 0.1 to 0.1.</bibtext> </blist> <blist> <bibtext> We use pre‐program data for those covariates that are not measured at baseline: birth weight, low birth weight, Apgar score at 1 minute, Apgar score at 5 minutes, age of the mother at birth, number of prenatal controls, gestational weeks, and number of previous pregnancies.</bibtext> </blist> <blist> <bibtext> Among the few variables that are unbalanced, the number of previous pregnancies is the most expected one. This is because families with more children have a lower income per capita and are therefore more likely to receive the PANES program.</bibtext> </blist> <blist> <bibtext> The estimation is performed using pre‐program data and considers the optimal bandwidth obtained in Table 2.</bibtext> </blist> <blist> <bibtext> We checked these correlations for other educational outcomes, and the conclusion is the same.</bibtext> </blist> <blist> <bibtext> Note that the number of observations in each regression changes according to the bandwidth. For the same sample, the number of observations changes depending on whether we use controls or not. These changes do not always go in the same direction. In Tables A8 and A9 in the Appendix, we report results using specific bandwidths with a fixed number of observations.</bibtext> </blist> <blist> <bibtext> This method was first formalized by Grembi et al. ([24]), but others have used similar empirical strategies in prior literature. Grembi et al. ([24]) proposed and verified a set of diagnostic tests for this design, referring to this method as a "difference‐in‐discontinuity design." Identification rests on the difference between two cross‐sectional estimators rather than within‐unit variation in treatment assignment.</bibtext> </blist> <blist> <bibtext> We include an equivalent set of control variables as those used in Amarante et al. ([5]).</bibtext> </blist> <blist> <bibtext> We do not use a CCT bandwidth for these estimations given that the equation we estimate does not correspond to a traditional regression discontinuity design.</bibtext> </blist> <blist> <bibtext> Note, however, that Amarante et al. ([5]) did not find an effect of PANES on low birth weight when using a regression discontinuity strategy.</bibtext> </blist> <blist> <bibtext> Amarante et al. 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International Journal of Epidemiology, 40 (4), 1008 – 1018. https://doi.org/10.1093/ije/dyr082</bibtext> </blist> </ref> <aug> <p>By Juanita Bloomfield and José María Cabrera</p> <p>Reported by Author; Author</p> <p></p> <p>Juanita Bloomfield is an Assistant Professor at Universidad de Montevideo, Dr. Prudencio de Pena 2544, 11600, Montevideo, Uruguay (email: j.bloomfield@um.edu.uy).</p> <p>José María Cabrera is an Assistant Professor at Universidad de Montevideo, Prudencio de Pena 2544, 11600, Montevideo, Uruguay (email: jmcabrera@um.edu.uy).</p> </aug> <nolink nlid="nl1" bibid="bib21" firstref="ref2"></nolink> <nolink nlid="nl2" bibid="bib20" firstref="ref3"></nolink> <nolink nlid="nl3" bibid="bib34" firstref="ref6"></nolink> <nolink nlid="nl4" bibid="bib32" firstref="ref7"></nolink> <nolink nlid="nl5" bibid="bib35" firstref="ref8"></nolink> <nolink nlid="nl6" bibid="bib26" firstref="ref10"></nolink> <nolink nlid="nl7" bibid="bib10" firstref="ref11"></nolink> <nolink nlid="nl8" bibid="bib25" firstref="ref12"></nolink> <nolink nlid="nl9" bibid="bib23" firstref="ref13"></nolink> <nolink nlid="nl10" bibid="bib27" firstref="ref16"></nolink> <nolink nlid="nl11" bibid="bib17" firstref="ref17"></nolink> <nolink nlid="nl12" bibid="bib30" firstref="ref20"></nolink> <nolink nlid="nl13" bibid="bib12" firstref="ref23"></nolink> <nolink nlid="nl14" bibid="bib29" firstref="ref28"></nolink> <nolink nlid="nl15" bibid="bib19" firstref="ref30"></nolink> <nolink nlid="nl16" bibid="bib15" firstref="ref31"></nolink> <nolink nlid="nl17" bibid="bib31" firstref="ref35"></nolink> <nolink nlid="nl18" bibid="bib22" firstref="ref44"></nolink> <nolink nlid="nl19" bibid="bib18" firstref="ref48"></nolink>
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Items – Name: Title
  Label: Title
  Group: Ti
  Data: Long-Term Impacts on Education of a Cash Transfer during Early Life
– Name: Language
  Label: Language
  Group: Lang
  Data: English
– Name: Author
  Label: Authors
  Group: Au
  Data: <searchLink fieldCode="AR" term="%22Juanita+Bloomfield%22">Juanita Bloomfield</searchLink> (ORCID <externalLink term="https://orcid.org/0000-0002-1230-0719">0000-0002-1230-0719</externalLink>)<br /><searchLink fieldCode="AR" term="%22José+María+Cabrera%22">José María Cabrera</searchLink>
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  Group: Src
  Data: <searchLink fieldCode="SO" term="%22Journal+of+Policy+Analysis+and+Management%22"><i>Journal of Policy Analysis and Management</i></searchLink>. 2026 45(1).
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  Label: Availability
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  Data: Wiley. Available from: John Wiley & Sons, Inc. 111 River Street, Hoboken, NJ 07030. Tel: 800-835-6770; e-mail: cs-journals@wiley.com; Web site: https://www.wiley.com/en-us
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  Data: Y
– Name: Pages
  Label: Page Count
  Group: Src
  Data: 21
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  Label: Publication Date
  Group: Date
  Data: 2026
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  Label: Document Type
  Group: TypDoc
  Data: Journal Articles<br />Reports - Research
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  Label: Descriptors
  Group: Su
  Data: <searchLink fieldCode="DE" term="%22Foreign+Countries%22">Foreign Countries</searchLink><br /><searchLink fieldCode="DE" term="%22Financial+Support%22">Financial Support</searchLink><br /><searchLink fieldCode="DE" term="%22Welfare+Services%22">Welfare Services</searchLink><br /><searchLink fieldCode="DE" term="%22Poverty+Programs%22">Poverty Programs</searchLink><br /><searchLink fieldCode="DE" term="%22Young+Children%22">Young Children</searchLink><br /><searchLink fieldCode="DE" term="%22Program+Effectiveness%22">Program Effectiveness</searchLink><br /><searchLink fieldCode="DE" term="%22Educational+Attainment%22">Educational Attainment</searchLink><br /><searchLink fieldCode="DE" term="%22Body+Weight%22">Body Weight</searchLink><br /><searchLink fieldCode="DE" term="%22Infants%22">Infants</searchLink>
– Name: Subject
  Label: Geographic Terms
  Group: Su
  Data: <searchLink fieldCode="DE" term="%22Uruguay%22">Uruguay</searchLink>
– Name: DOI
  Label: DOI
  Group: ID
  Data: 10.1002/pam.22663
– Name: ISSN
  Label: ISSN
  Group: ISSN
  Data: 0276-8739<br />1520-6688
– Name: Abstract
  Label: Abstract
  Group: Ab
  Data: We evaluate the long-term effects of receiving the Uruguayan "Plan de Atención Nacional a la Emergencia Social" (PANES), a large unconditional cash transfer program, on outcomes for young and unborn children. We use a rich dataset that matches program administrative data to vital natality data and educational records 8 to 12 years after the beginning of the program. Overall, we find small and barely significant effects on educational attainment and delay. Among children exposed to the program during early childhood (between ages 0 and 5), the results show significant beneficial effects for those with low birth weight.
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  Group: Date
  Data: 2026
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  Data: EJ1493921
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    Identifiers:
      – Type: doi
        Value: 10.1002/pam.22663
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      – Text: English
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        PageCount: 21
    Subjects:
      – SubjectFull: Foreign Countries
        Type: general
      – SubjectFull: Financial Support
        Type: general
      – SubjectFull: Welfare Services
        Type: general
      – SubjectFull: Poverty Programs
        Type: general
      – SubjectFull: Young Children
        Type: general
      – SubjectFull: Program Effectiveness
        Type: general
      – SubjectFull: Educational Attainment
        Type: general
      – SubjectFull: Body Weight
        Type: general
      – SubjectFull: Infants
        Type: general
      – SubjectFull: Uruguay
        Type: general
    Titles:
      – TitleFull: Long-Term Impacts on Education of a Cash Transfer during Early Life
        Type: main
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      – PersonEntity:
          Name:
            NameFull: Juanita Bloomfield
      – PersonEntity:
          Name:
            NameFull: José María Cabrera
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            – D: 01
              M: 01
              Type: published
              Y: 2026
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            – Type: issn-print
              Value: 0276-8739
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              Value: 1520-6688
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              Value: 45
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            – TitleFull: Journal of Policy Analysis and Management
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