When the Money Runs Out:Do Cash Transfers Have Sustained Effects on Human Capital Accumulation?
March 30, 2019
Sarah Baird
Department of Global HealthMilken Institute School of Public HealthGeorge Washington University
950 New Hampshire Ave. NW
Washington, DC 20052
sbaird@gwu.edu
202-994-0270
Craig McIntosh
School of Global Policy and Strategy
University of California, San Diego
9500 Gilman Dr.
La Jolla, CA 92093-0519
ctmcintosh@ucsd.edu
858-822-1125
Berk Özler
Development Economics Research Group
The World Bank
1818 H Street NW, Mail Stop MC3-306
Washington, DC 20433.
Phone: 202-458-5861
Email: bozler@worldbank.org

When the Money Runs Out:Do Cash Transfers Have Sustained Effects on Human Capital Accumulation?*
Sarah Baird, Craig McIntosh, and Berk Özler
March 30, 2019
Abstract
The five-year evaluation of a cash transfer program targeted to adolescent females points to boththe promise and limitations of cash transfers for persistent welfare gains. Conditional cash transfers
produced sustained improvements in education and fertility for initially out-of-school females butcaused no detectable gains in other outcomes. Significant declines in HIV prevalence, pregnancy
and early marriage observed during the program among recipients of unconditional cash transfers(UCTs) evaporated quickly after the cessation of support. However, children born to UCT
beneficiaries during the program had significantly higher height-for-age z-scores at follow-up
pointing to the potential importance of cash during critical periods.
Keywords: Cash Transfers, Medium-term Impacts, Human capital, Adolescents
JEL Codes: C93, I15, I21, I38, J12, J13* Sarah Baird (corresponding author), email: sbaird@gwu.edu, George Washington University; Craig McIntosh,email: ctmcintosh@ucsd.edu, University of California, San Diego; Berk Özler, email: bozler@worldbank.org, The
World Bank. We thank seminar and conference participants at the Center for the Study of African Economies,
Columbia University, CU Denver, Georgetown University, IFPRI, Mannheim, McGill University, Middlebury
College, Monash Development Workshop, Oregon State University, Otago Development Workshop, Otago
International Health Research Network, Labor Econometrics Workshop, PopPov Annual Research Conference,
University of Maryland, University of Oklahoma, University of Oregon, University of Southern California, Universityof California, Berkeley, University of California, Los Angeles, Washington Area Development Economics
Symposium, Yale University, and the World Bank. We thank everyone who provided this project with great fieldwork
and research assistance and are too numerous to list individually. We gratefully acknowledge funding from the Global
Development Network, the Bill and Melinda Gates Foundation, 3ie, NBER Africa Project, and the World Bank.
Ethical review committees at the National Health Sciences Research Council (Malawi, Protocol #569) the Universityof California at San Diego (USA, Protocol #090378), and George Washington University (USA, Protocol #061037)
approved the study design. The trial is registered at AEA RCT Registry (#AEARCTR-0000036). The findings,
interpretations, and conclusions expressed are entirely those of the authors.

21. INTRODUCTION
The past decade has witnessed an impressive growth in the number, volume, and types ofcash transfer programs in developing countries. A rigorous evidence base has shown that cashtransfers can have significant effects on household consumption and educational attainment in the
short-run, even if the poor receive these transfers with few strings attached (Fiszbein et al. 2009;
Baird et al. 2013; Haushofer and Shapiro 2016; Garcia and Saavedra 2017; and Molina-Millán etal. 2018a). Furthermore, several working papers and journal articles that have been published in
the past couple of years point to some robust evidence of longer-term effects on schooling, but
mixed findings on other important outcomes, such as skills, employment, and earnings (MolinaMillán et al. 2018a, for a review). It is still an open question whether such programs can improve
the wellbeing of their young beneficiaries when they become adults – after the cessation of support.
This question is particularly pertinent for Conditional Cash Transfer (CCT) programs, which arebuilt on the premise that they not only fight current poverty, but also promote human capital
accumulation for the next generation. As cash transfer programs continue to grow as major
vehicles for social protection, it is important to understand if these programs break the cycle ofintergenerational poverty, or whether the benefits simply evaporate when the money runs out.1
This paper fits into this growing literature and attempts to contribute to it in two importantways. First, it presents experimental estimates of the impact of a two-year CCT program targetedat adolescent females in Malawi more than two years after the program ended (or four to five years
after baseline) – using both a pure control group that never received treatment and anothertreatment arm that was offered equal-sized unconditional cash transfers (UCT). Second, it uses
data on a rich set of outcomes (education, childbearing and marriage, health, labor market
outcomes, empowerment, and subjective wellbeing) for the target population of young females, aswell as information about children born to them during the study period.2 The resulting analysis is

1

There is a recent wave of transfer programs, generally conducted by NGOs, which aim to lift households out ofpoverty using larger lump-sum transfers during a limited period of support (Bandiera et al. 2017a; Banerjee et al.
2015; Haushofer and Shapiro 2016, Haushofer and Shapiro 2018). Evaluations of these programs are generally
concerned with current poverty reduction rather than human capital accumulation among children. As such, while thequestion of sustained effects is also pertinent for these studies, they are less relevant for our examination of longerterm impacts on adolescent beneficiaries.
2
We also collected data on the husbands of married respondents, but chose to exclude that analysis in this paper basedon previous feedback from reviewers. Given that there is significant attrition in our husband data and many of theadolescents are still transitioning into marriage (only 40% of the baseline schoolgirls are married two years after the
program compared with 81% of baseline dropouts), the detailed secondary analysis required goes beyond the scopeof this paper. For preliminary analysis of these data, the reader can refer to Baird, McIntosh and Özler (2016).

3

a comprehensive assessment of the relative effects of CCTs and UCTs targeted to adolescents for
two years during a period of transition into adulthood – conducted more than two years after they
stopped receiving the transfers.3
For any intervention to have a sustained effect, it needs to lead to an increase in the stockof some asset that produces a stream of returns in the future, i.e. some accumulation of capital –whether it takes the form of human, physical, or social capital. However, the causal pathway fromprogram implementation to final outcomes can be circuitous. For example, a program that provides
cash grants to groups of unemployed youth for income generating activities may have lasting
effects on earnings through the accumulation of physical (productive assets) and human(vocational skills) capital (Blattman, Fiala and Martinez 2014). Alternatively, large unconditional
cash grants to poor households may increase future earnings by increasing investments in
productive assets, such as livestock (Haushofer and Shapiro 2016).4 Still, small monthly cashtransfers over a long period of time may lead to increased consumption after beneficiaries exit the
program by increasing savings and investments in small-scale agriculture or non-farm activity(Gertler, Martinez and Rubio-Codina 2012, Handa et al. 2018) or by stimulating entrepreneurial
activity (Bianchi and Bobba 2013).
For programs targeting younger people, the causal pathway to improved welfare over thelong run is more likely to be human capital accumulation, either in the form of education and skillsor health – especially reproductive and sexual health for adolescent females. Even when young
women attain higher schooling and delay fertility and marriage, low quality education, credit
constraints, and low demand for skilled labor can stunt income gains. Without economic

Cash transfers during adolescence may be particularly effective as this is a critical period to expand one’s capabilities
by investing in human capital. In fact, adolescent girls are viewed as a key demographic target group to successfully
break the intergenerational transmission of poverty in developing countries (Levine et al. 2008). Unfortunately, formany boys and girls in developing countries, adolescence entails a fleeting transition from childhood to adulthood,when they are suddenly expected to “behave as adults even though they are not biologically, cognitively, or
emotionally ready to assume adult responsibilities” (Naudeau, Hasan and Bakilana 2015). Adolescent females inparticular face a multitude of hazards – ranging from school dropout, to child marriage and teen pregnancy, to physicaland mental health problems, to gender based violence (Baird and Özler 2016). Young people’s capabilities andfunctioning (Heckman and Corbin 2016) during this period not only have immediate consequences to their own lives,
but also longer-term benefits to their offspring and communities at large (Lloyd and Young 2009; Duflo 2012).
Interventions that help adolescent girls reach their full potential by increasing their education, improving their skills,
and delaying childbearing have the potential to create a virtuous cycle that improves health, especially child health,and women’s empowerment – ultimately leading to higher economic growth (Canning, Raja and Yazbeck 2015).
4
It should be noted that, despite promising impacts in the shorter-run, longer-term evaluations of both of these
programs indicated convergence between the treatment and control groups with respect to employment, earnings, andconsumption (Haushofer and Shapiro 2018; Blattman, Fiala, and Martinez 2018).
34

independence, potential gains in women’s agency, intra-household bargaining power, andempowerment are foregone.
Programs targeted to adolescent females may not only delay marriage and childbearing but
may also benefit the development of their own children. A distinct and mostly U.S.-based
literature, largely using quasi-experimental methods, has examined the very long-term effects ofbeing exposed to cash, ‘near cash,’ or other safety net programs during childhood (e.g. Currie andAlmond 2011; Aizer et al. 2016; Hoynes, Schanzenbach and Almond 2016; Chetty, Hendren andKatz 2016) and has demonstrated beneficial effects on a host of outcomes as adults.
In this paper, we report the effects of a two-year cash-transfer experiment more than two
years after it ended, tracking a broad range of outcomes for females aged 18-27 at follow-up.5 Our
earlier work has demonstrated the short-term effectiveness of these transfers in improving schoolparticipation and test scores, as well as reducing the incidence of pregnancy, marriage,
psychological distress, and sexually transmitted infections during adolescence, indicating thepossibility of finding longer-term improvements in well-being as young adults (Baird, McIntosh
and Özler 2011; Baird et al. 2012; Baird, De Hoop and Özler 2013). Here, following a pre-analysis
plan, we first examine human capital accumulation, marriage and fertility, labor market outcomes,
and empowerment among the beneficiaries to assess the persistence of the short-term effects. Then,as most of the study participants had children at the latest follow-up, we examine their children’s
physical development using anthropometric measurements.
We find that the short-term improvements in the UCT arm observed during the program
failed to translate into increased welfare in the longer-term. Substantial reductions in teen
marriages, total live births, and HIV infections, as well as improvements in psychologicalwellbeing and nutritional intake observed at the end of the program were no longer apparent two
years later.6 We observe a spike in marriages and a baby boom among UCT beneficiaries
immediately following the end of the program, who reported lower levels of empowerment
compared with both the CCT and the control groups. However, consistent with improved physical,
nutritional, and mental health during the program, we find suggestive evidence of improved heightfor-age z-scores (HAZ) among children born to UCT recipients during the program.

5

At baseline, the target population was never-married females, aged 13-22.
This finding of quick convergence following short-term gains is consistent with, among others, Brudevold-Newman
et al. (2017) and Hicks et al. (2018).
6

5

CCTs, on the other hand, caused sustained effects on school attainment, incidence ofmarriage and pregnancy, age at first birth, total number of births, and desired fertility – but only
among the stratum of adolescent females who had already dropped out of school at baseline andwere all assigned to CCTs. Conditional transfers were highly effective in allowing a very large
share of this group to return to school.7 However, even in this group, we find no gains in otherimportant outcomes, such as individual earnings, per capita household consumption, subjective
wellbeing, health, or empowerment. Among the stratum that was enrolled in school at baseline,
while we cannot rule out some positive impacts on education and competencies, CCTs did nothave any observable effects, positive or negative, on longer term outcomes of empowerment andemployment. One reason behind these findings may be that the transfers were mostly inframarginal
with respect to school attainment: 88% of the control group in this stratum completed primaryschool two years after the end of the program. Comparing the CCT and UCT groups in this stratum,
we find that none of the statistically significant short-term differential impacts between the twogroups remain in the longer-run – apart from age at first marriage being higher and empowerment
levels lower in the UCT arm.
Our paper speaks to a small number of distinct literatures. First, it adds to a growing bodyof work on the medium- to long-term effects of cash transfer programs in developing countries.8
A number of longer-term evaluations of cash transfers programs (mostly of CCTs) indicate thatwhile cash transfer programs might improve school attainment among adolescent beneficiaries,
evidence of longer-term gains in terms of learning, employment, and income are mixed as they
become young adults (Baez and Camacho 2011; Behrman, Parker and Todd 2011; Barham,
Macours and Maluccio 2013; Filmer and Schady 2014; Araujo, Bosch and Schady 2016; Cahyadi
et al. 2018; Molina-Millán et al. 2018b). Our finding that CCT programs can substantially increase
school attainment among vulnerable populations with at best mixed effects on test scores,
cognitive skills, employment rates, or earnings is consistent with these studies.9
7

These findings align nicely with Duflo, Dupas and Kremer (2017) who find that by age 25 Ghanaian students who
were offered a secondary school scholarship were 26 percentage points more likely to complete secondary school andhad 0.217 fewer children—again suggesting the importance of the magnitude of the education effect.
8
It also builds on Baird, McIntosh and Özler (2011) and adds to the small literature that directly compares CCTs with
UCTs either experimentally (Akresh et al. 2013; Benhassine et al. 2015) or quasi-experimentally (Schady and Araujo
2008; de Brauw and Hoddinott 2011; Attanasio et al. 2015).
9
While the evidence on longer-term gains from CCT programs is mixed, especially outside of schooling (MolinaMillán 2018a) and others have also struck a cautious tone about the transformative effects of social protection
programs more generally (Molyneux, Jones and Samuels 2016), some studies do find evidence of promising longerterm gains. Barrera-Osorio et al. (forthcoming) find that a forced savings treatment attached to a traditional schooling6Second, our study contributes to a large literature on the effects of programs that support
pregnant women and young children. Policies for child development often target the first 1,000
days from conception to the second birthday (Barham, Macours and Maluccio 2013). What is
novel in our study is that we examine the effects of targeting cash transfers to adolescent femalesof childbearing age and provide evidence for the important policy question on the timing ofinterventions for young women to protect early childhood development.10 Our findings suggestthat unconditional income support for adolescent girls and young women of childbearing age mightcause significant increases in height-for-age z-scores of their children. They are also consistent
with Cahyadi et al. (2018), which finds that children 0-5 who have been exposed to Indonesia’s
CCT program are substantially less likely to be stunted or severely stunted.11
The remainder of this paper is structured as follows. Section 2 describes the study setting,study design, and data collection instruments. Section 3 presents our estimation strategy. Sections
4 presents program impacts on the core respondents, followed by an examination of some key
characteristics of their children. Section 5 concludes.

2. STUDY SETTING, DESIGN, AND DATA SOURCES
2.1 Study Setting
The “Schooling, Income, and Health Risk” study (SIHR) follows young women who wereenrolled as never-married adolescents (aged 13-22) in Zomba, Malawi in 2007. We interviewed
them for the fourth time in 2012 – approximately five years after baseline and more than two years
after the cessation of the cash transfer experiment in December 2009, tracking the adolescents as
CCT program in Bogota increases tertiary enrollment and graduation, but the authors do not have data on otheroutcomes. Parker and Vogl (2018) finds that exposure to Mexico’s CCT program, PROGRESA, increased school
attainment by 1.3 years for both sexes, while finding statistically significant increases in labor market participationand earnings only among females. Barham, Macours and Maluccio (2018a) focus on the differential exposure of boys
to Nicaragua’s CCT program between the ages of 9 and 12 and find that previously demonstrated short-term increases
in schooling are sustained after 10 years and there are substantial gains in learning. Barham, Macours and Maluccio(2018b) does the same for girls and finds that differential exposure to CCT does not lead to schooling gains, but it
does cause reductions in fertility and increases in economic activity and earnings. The evaluation of a school-based
intervention in Kenya that provided school uniforms found significant reductions in school dropout, pregnancy, andmarriage among girls in the short- and medium-run; and school attainment, marriage, and childbearing by age 16 in
the longer-run (Duflo, Dupas and Kremer 2015). However, another program that distributed school uniforms in Kenya
found that the short-term effects on school absenteeism led to no substantive positive long-term education impacts(Evans and Ngatia 2018).
10
Currie and Almond (2011) state “…one of the more effective ways to improve children's long-term outcomes might
be to target women of child bearing age in addition to focusing on children after birth.”11
See Manley, Gitter and Slavchevska (2013) for a review of the effects of cash transfers on children’s nutritional
status in low- and middle-income countries (LMICs).

7

many of them went on to establish their own families. These longitudinal data paint a very rich
picture of the transition from adolescence into adulthood in this context. By 2012, in the control
group, the study stratum that had dropped out of school at baseline had effectively completed theirschooling with an average of a seventh-grade education; 81% were married, 92% had beenpregnant, and only 6% had spent any time in self-employment or paid work during the past week.
More than one in eight (13.5%) had been infected with HIV. The stratum of baseline schoolgirls
is better-off and younger, and therefore had not proceeded as far in their transition to adulthood:in 2012, their average years of schooling was 10.4 and consistently increasing over the study
period, with only 40% ever married, 50% ever pregnant, and 5.5% HIV-positive.
In the latest follow-up survey of the study sample, which was more than two years after
the cessation of cash transfers, we attempted to trace the pathways through which experimentallyinduced changes in human capital may translate into longer-term changes in outcomes. Zomba isan almost exclusively agricultural economy characterized by low educational attainment and few
opportunities for formal employment. As of 2009, this district was the third poorest in Malawi (inour sample, real monthly per-capita exchange rate comparable consumption in 2008 was USD
20.6). Secondary school completion rates are low – in our sample, among baseline schoolgirls,
half of whom had completed primary school at baseline, only 17.0% had completed secondary
school as of 2012. Although most adults 15 and over participate in some form of employment, themajority do not receive a formal income. In 2008, only 6% of the adult population in Zomba
received a formal income (Zomba City Assembly 2009), a number that is reflected in our data with
6% of baseline dropouts and 3% of baseline schoolgirls participating in any formal work. This
context is typical for many parts of rural Africa, and, hence, is an important environment in which
to understand the constraints adolescents face as they transition to adulthood.
2.2 Study Design
Our study began by listing all eligible households within 176 Enumeration Areas (EAs) of
the 550 EAs in Zomba District, identifying households with never-married females, aged 13-22
year-old, and dividing this target population into two main strata: those who were already out ofschool at baseline (baseline dropouts) and those who were still in school at baseline (baselineschoolgirls). Baseline dropouts comprised only 15% of target population, so were all recruited into
the study. Baseline schoolgirls were sampled into the study at probabilities increasing in age andrural status. These two strata have always been analyzed separately for three main reasons: (a) we8do not have the UCT experiment among the baseline dropouts, (b) the CCT experiment acts
differently for these two groups (bringing dropouts back into school while keeping schoolgirls
from dropping out) and (c) the two groups look very different based on their observable baselinecharacteristics. Following the pre-analysis plan, we analyze them separately in this paper as well.
Treatment was assigned first at the enumeration area (EA) level; 88 to treatment and 88 tocontrol. All baseline dropouts in treatment EAs received CCTs, while we experimented with
attaching conditions to the cash transfers within the larger cohort of baseline schoolgirls. For them,
46 EAs were assigned to CCTs, 27 were assigned to UCTs, and 15 were assigned to receive notransfers to study spillovers (from baseline dropouts in those EAs). The amount of money received
by the household head was randomized between $4 and $10 at the EA level, and the core
respondents were assigned their own individual transfer amounts – ranging from $1 and $5 – in a
public lottery.12 The share of eligible girls offered cash transfers was randomly varied acrossclusters to estimate spillover effects as a function of treatment intensity. Offer letters were
distributed in December 2007, payments began in February 2008 and continued through the endof 2009.13 Four rounds of data took place: Round 1-Baseline (2007), Round 2 (2008), Round 3(2010), and Round 4 (2012). Figure I presents an illustration of the study design, and a moredetailed description of the experiment can be found in (Baird, McIntosh and Özler 2011).14
Girls receiving UCTs simply had to show up at a local distribution point each month topick up their transfers. Monthly school attendance for all girls in the CCT arm was checked andpayment for the following month was withheld for any student whose attendance was below 80%of the number of days school was in session for the previous month. However, participants were
never removed from the program for failing to meet the monthly 80% attendance rate, meaning

12

The average total transfer to the household of $10/month for 10 months a year is nearly 10% of the average
household consumption expenditure of $965 in Malawi in 2009 (World Bank, 2010). This falls in the range of cashtransfers as a share of household consumption (or income) in other countries with similar CCT programs. The transfers
were offered to all eligible girls in our target demographic and were not targeted by poverty status.
13
In experiments like SIHR, it is important to try to understand what the beneficiaries expected as to the program’s
timing and duration (Bazzi, Sumarto and Suryahadi 2015). When the initial offers were made, the beneficiaries weretold that the program only had funding for one year, but that efforts were being made to extend it into a two-year
program. Towards the end of the first year, upon successfully obtaining additional funding, we circulated new offer
letters informing the beneficiaries that the program would be continued for one more year, but not more. This message
was repeated regularly at the cash distribution points by the program staff during the second and final year of theintervention.
14
The size of the transfers, the identity of the recipients, or the intensity of treatment within the cluster did not prove
to be influential on the primary outcomes of interest. Because these were randomized across the control, CCT, andUCT arms, estimates of average treatment effects remain highly robust to these controls.

9

that if they subsequently had satisfactory attendance, their payments would resume. Other design
aspects of the program were kept identical to be able to isolate the marginal effect of imposing aschooling conditionality on outcomes of interest among baseline schoolgirls.15

2.3 Data Sources and Outcomes
The focus of this paper is data collected in Round 4, which took place in 2012, more than
two years after the end of the intervention. However, to provide context for Round 4 findings, we
also present impacts on the same outcomes, when available, for data collected during Rounds 2
and 3. Focusing on the core respondent, the data sources include household surveys (all rounds),
biomarker data collection on HIV (Round 2-4) and Anemia (Round 4), and competencies (Round4). In Round 4, data collection also included anthropometrics (children aged 60 months or under).
The household surveys at each round consisted of a multi-topic questionnaire administered
to the households in which the core respondents resided during the data collection period. They
consisted of two parts: one that was administered to the head of the household and the otheradministered to the core respondent. The former collected information on the household roster,dwelling characteristics, household assets and durables, shocks, and consumption. The survey
administered to the core respondent collected detailed information about her family background,schooling status, health, dating patterns, sexual behavior, fertility, marriage, labor market
outcomes, and empowerment.
The Round 4 household survey also included a test of basic labor market skills of the core
respondent, which we termed “competencies.” It included reading and following instructions toapply fertilizer; making correct change during a hypothetical market transaction; sending a text
message and using a calculator on a mobile phone, and calculating profits in a hypothetical trading
scenario. As Round 4 was focused more on the transition into adulthood and labor markets, as
opposed to the school attainment and learning focus in Round 3, this test was designed to replace
the reading comprehension, math, and cognitive skills tests utilized in Round 3, intended to serve
as a measure of a more practical set of skills that might be influenced by increased schooling andneeded in the labor market.

15

For households with girls eligible to attend secondary schools at baseline, the total transfer amount was adjusted
upwards by an amount equal to the average annual secondary school fees in the conditional treatment arm. Thisadditional amount ensured that the average transfer amounts offered in the CCT and UCT arms were identical and theonly difference between the two groups was the “conditionality” of the transfers on school attendance.

10Home-based voluntary counseling and testing for HIV (for core respondents during Rounds
2-4) was conducted by Malawian nurses and counselors certified in conducting rapid HIV tests
through the Ministry of Health HIV Unit HCT Counselor Certification Program. In addition, theytested for hemoglobin of the core respondent and measured the height and weight of all children
aged 60 months or younger.
Prior to the analysis of data from Round 4, a pre-analysis plan was registered at the AEA
RCT Registry (AEARCTR-0000036; https://www.socialscienceregistry.org/trials/36).16 Our
outcomes cover six pre-specified domains for the core respondent – education and competencies,
marriage and fertility, health and sexual behavior, empowerment and aspirations, employment andwages, and consumption.17 We deviate from the pre-analysis plan for the child outcomes giventhat the more complicated methodology needed to address causal identification was not adequately
addressed in the pre-analysis plan. The analysis of program impacts on child height should thus beconsidered exploratory.

3. ESTIMATION STRATEGY
In this section, we discuss the experimental estimation strategy used to examine program
impacts on core respondents. The causal identification of program impacts on children’s outcomesis more challenging and the estimation strategy used to analyze these outcomes is discussed in
Section 4.6 and Appendix A.
To estimate intention-to-treat effects of the program in each treatment arm on our primary
outcomes by stratum, we employ a simple reduced-form linear model:
𝑌𝑖𝑐 = 𝛼 + 𝛾 𝑐 𝑇𝑐𝑐 + 𝛾 𝑢 𝑇𝑐𝑢 + 𝛽𝑋𝑖𝑐 + 𝜀𝑖𝑐(1)where 𝑌𝑖𝑐 is an outcome variable for core-respondent i in cluster c, 𝑇𝑐𝐶 and 𝑇𝑐𝑈 are binary indicatorsfor offers in the CCT and the UCT clusters, respectively, and Xic is a vector of baselinecharacteristics. Note that for baseline dropouts we only have the CCT binary indicator. The

16

Many of our outcomes are in the form of indexes that are constructed using the following rubric: First, we ensured
that all sub-questions are aligned so that higher scores always have a consistent meaning (good or bad). We thencalculated the mean and standard deviation of the responses to each sub-question in the control group – separately forbaseline schoolgirls and baseline dropouts. We then normalized each sub-question by subtracting the mean anddividing by the standard deviation. Finally we constructed (and then normalized) the raw mean of the normalized
variables for all sub-questions within a family of variables to create the final index.
17
A detailed description of all outcomes specified in the pre-analysis plan can be found here:
https://drive.google.com/file/d/1hvI79ltywocFr-pafqz8_Dtg2ZXNhcHd/view.

11standard errors 𝜀𝑖𝑐 are clustered at the EA level, which account for both the design effect of our
EA-level treatment and the heteroskedasticity inherent in the linear probability model.
In all regressions, we include baseline values of the following pre-specified variables ascontrols: a household asset index, highest grade attended, a dummy variable for having started
sexual activity, and dummy variables for age in years. These variables were chosen because they
are strongly predictive of schooling outcomes, hence improving the precision of the impact
estimates. We also include indicators for the strata used to perform block randomization – Zomba
Town, within 16 kilometers of the town, and beyond 16 kilometers (Bruhn and McKenzie 2009).
Age- and stratum-specific sampling weights are used to make the results representative of thetarget population in the study area.
Table I presents means and standard deviations for nine individual or household
characteristics for the study sample at baseline by strata and treatment assignment. As this paper
is mainly about program effects more than two years after the end of cash transfers, we conduct
all analysis among those who were successfully interviewed in Round 4, which maximizes sample
size for the estimation of longer-term impacts.18 Columns 1 and 2 show descriptive statistics forbaseline dropouts, who are older than baseline schoolgirls and come from more disadvantaged
backgrounds: for example, 44.5% of the control group had started childbearing at baselinecompared to only 2.1% of baseline schoolgirls. In addition to the fact that all baseline dropouts
are out of school at baseline and never married, there are no statistically significant differences
between the CCT and the control groups for the variables presented in Table 1. Nor are there any
differences between the two treatment groups and the control group among baseline schoolgirls,
but the UCT group is, on average, older and has attended higher grades than the CCT group atbaseline. Note that this imbalance existed at baseline and is not a result of differential attrition(Baird, McIntosh and Özler 2011). Pre-specified baseline controls used in all impact regressions
described above include these two variables. Joint tests of orthogonality presented at the bottomof Table 1 confirm these findings.

18

Conducting the analysis among the Round 4 sample implies that the Round 2 and Round 3 samples are smaller thanthe Round 4 sample in the analysis. For example, to be included in the Round 3 analysis of impacts, a subject had tobe successfully interviewed in both Rounds 3 and 4. In addition to maximizing the sample for Round 4 analysis, whichis the focus of this paper, this allows us to demonstrate that the Round 2 and Round 3 impacts, which were reported
in earlier publications, hold in this sub-sample and provides some reassurance that differential attrition is notsubstantially affecting our findings at Round 4.

12

Appendix Table S1 provides tracking data for Round 4, overall and then for baseline
dropouts and baseline schoolgirls. We found over 94% of the sample and surveyed close to 90%of the overall study sample split as follows across the strata and treatment arms: baseline dropouts
lost to Round 4 follow-up: 15.7% in the control, 16.4% in treatment; baseline schoolgirls lost to
Round 4 follow-up: 12.5% in the control, 7% in the CCT arm, and 6.7% in the UCT arm. The
difference between found and surveyed is largely due to refusals, which were higher among thecontrol group. The most common reason for refusal (which are clearly documented in the data) is
no longer seeing a benefit of the study, and thus not suggestive of improved or worse outcomesfor respondents who refused. Examining further the data we have on the 6% completely lost tofollow-up (as opposed to found but refused to participate), general location information exists for
165 (or 86%) of the 192 remaining study participants. Coding their new location as urban if they
moved to the two main cities in Malawi (Lilongwe or Blantyre) or overseas, we find no statisticallysignificant impact of treatment on moving to urban areas in this group (in fact, the coefficientestimates are negative). While these data on our full sample partly mitigates concerns over null
findings being driven by differential attrition (of successful treatment beneficiaries having movedaway), we proceed with a detailed analysis of attrition.
Table II examines attrition for the same sample of core respondents who were successfullyinterviewed in Round 4 – first for baseline dropouts, then baseline schoolgirls. Attrition two years
after the end of the cash transfer program in terms of having a completed survey is 15.7% in thecontrol group among baseline dropouts and this level of attrition is not differential in the CCT arm(column 1). However, interacting attrition with the same pre-specified baseline adjustments usedthroughout the paper, we find that these interactions are jointly significant (column 2) – primarily
because CCT beneficiaries in urban areas, which constitutes less than 20% of our sample, weremore likely to be lost to follow-up19. Attrition in the control group among baseline schoolgirls isslightly lower at 12.5%, which is significantly higher than both the CCT and UCT arms (column
3). However, attrition in this stratum is not differential by baseline characteristics between
treatment and control, although the F-test for joint significance of UCT interactions is 0.101(column 4). This lack of interaction effect reflects the fact that the differential attrition is largely

19

Note that there are only 80 respondents total in this cell, so it is unlikely to alter impact findings. Moreover, for thesubset of those lost to follow-up for whom we have limited information, there is no indication of improved outcomes(they are either deceased, have a mental illness, no longer live in urban areas, or are married with no educational
qualification).

13

driven by higher likelihood of refusals in the control group. Furthermore, and importantly for our
experiment, there is no differential attrition between the CCT and UCT arms – either in levels or
by characteristics. Appendix Table A2 displays the coefficients of the probit regressions that
underlie the differential selection statistics provided in Table II and form the basis of the Inverse
Propensity Weights (IPW) used later in the paper.
We attempt to address some of the potential bias in impact estimates due to differential
attrition by treatment arm – either in levels (CCT and UCT among baseline schoolgirls) or inbaseline characteristics (CCT among baseline dropouts) by including a thorough analysis of therobustness of our impact estimates in Section 4.5 below. There, we present estimates reweighted
to account for attrition (IPW), upper and lower bounds on impact estimates for all primary
outcomes (Lee 2009), as well as adjustments using the techniques of Kling and Liebman (2004).
We also note that impact estimates from earlier follow-up rounds, which did not suffer fromdifferential attrition, replicate in the Round 4 sample used in this paper.20 These tests do rely on
certain assumptions, so results should be interpreted in that light.

4. RESULTS
We start by presenting the trajectory of program effects on outcomes in four domains,separately for baseline dropouts and baseline schoolgirls: education and competencies, marriage
and fertility, health, and, finally, labor market participation and empowerment.21

4.1 Education and Competencies
Table III presents program impacts on highest grade completed and competencies. Amongbaseline dropouts, CCTs led to an increase in highest grade completed of approximately 0.6 years,
which represents a 0.22 standard deviation (SD) increase by Round 4 (Panel A). As a result, theshare of beneficiaries with a Primary School Leaving Certificate (PSLC) increased by 5.8 and 8.1
percentage points in Rounds 3 and 4, respectively (Appendix Table S3, Panel A). Earlier gains in
20

Appendix Tables S9 and S10 show the impacts on the 5 primary outcomes measured in earlier rounds using the fullRound 2 and Round 3 samples when differential attrition – in levels or in baseline characteristics – was not an issue.
A comparison of these estimates to those restricted to the Round 4 sample reveals no substantive differences.
21
The reader should note that most of the one- and two-year impacts during and at the end of the program werereported in previous publications, which are clearly cited throughout the paper. What are new here are the findings
from two years after the end of the program. Presenting program impacts over time within each domain allows thereader to examine the trajectory of program effects and assess whether earlier impacts were sustained. Appendix tables
complement the main tables, presenting additional outcomes in all six pre-specified domains for the core respondent.

14

test scores of English reading comprehension, mathematics, and cognitive skills (Table III,columns 4-7) do not translate into a significant increase in scores on tests of basic labor market
skills, or “competencies,” such as following instructions to apply fertilizer or calculating change
in a market transaction (Table III, column 8; Appendix Table S3, Panel A, columns 10-15). This
result could reflect the fact that the competencies simply failed to measure variation in skills in a
useful way. However, we find this explanation unlikely as the variation in schooling and test scoresat the end of the intervention are strongly predictive of competencies two years later: for example,
a one-year increase in highest grade completed is associated with a 0.21 SD increase in the overall
competency score. Mechanically, this would imply an improvement of only 0.13 SD in the overall
competency score among baseline dropouts (0.621 x 0.21 = 0.13), which is twice as large as ourpoint estimate of 0.064 SD but well within the 95% confidence interval. Thus, we cannot rule out
meaningful sustained positive impacts on skills acquisition (or zero effect) for this group.
The results for baseline schoolgirls suggest little, if any, effect on school attainment orcompetencies in either treatment group (Table III, Panel B). Any significant effect in the CCTgroup at the end of the program was no longer detectable two years later. The reader should notethat the mean number of years completed in the control group is 10.4 in Round 4, at which point
88% of the control group had obtained a PSLC (Appendix Table S3, Panel B). Hence, while mostof the transfers to baseline schoolgirls were inframarginal with respect to primary school
completion, the cash transfer program did not cause any significant gains in secondary school
completion, either. Similarly, earlier gains in test scores in the CCT group did not translate into
improved competencies in the longer-run, with the only significant improvement seen in the UCTgroup being the ability to send a simple text message using a mobile phone. The likely explanation
for these results is that the small education gains seen in the short-run lead to small (non-detectable)
positive gains two years post program.22

4.2 Marriage and Fertility

22

We chose not to pre-specify self-reported enrollment as a primary outcome based on findings from Baird, McIntosh
and Özler (2011) that there is significant (and differential) misreporting in this variable. With this caveat in mind, we
do still find that core respondents in the CCT and UCT arm report enrollment rates that are approximately six
percentage points higher (p<0.05) than the control at Round 4. Baseline dropouts are also four percentage points more
likely to be enrolled in school (p<0.01), over a base of 2.4%.

15

As with the education outcomes, CCTs had large effects on marriage and fertility forbaseline dropouts that were sustained at Round 4 (Table IV, Panel A). They were 14.0, 15.7, and10.7 percentage points (pp) less likely to have been ever married at Rounds 2-4, respectively (allsignificant at 99% confidence). The corresponding reductions were 5.7, 8.1, and 4.0 pp for being
ever pregnant (all significant at 90% confidence or higher). Furthermore, there is a negative
fertility gradient among CCT beneficiaries, leading to a reduction of 0.147 total live births at
Round 4 (p-value < 0.001), which corresponds to a reduction of more than 10% (0.19 SD) and isconsistent with the reduction in stated desired fertility. Age at first marriage and first birth, both
calculated at the intensive margin, were similarly higher by 0.43 and 0.27 years, respectively.
Among baseline schoolgirls, CCTs had no effects on marriage and fertility at any point
during our study period (Table IV, Panel B). On the other hand, UCTs were very effective in
substantially reducing marriage and pregnancy rates among baseline schoolgirls during and at theend of the program (Baird, McIntosh and Özler 2011). Two years later, there are no longer any
differences in ever married, ever pregnant, total number of live births, or even age at first birth
between the UCT group and either the control group or the CCT arm. We find that the age at firstmarriage is delayed by half a year as of Round 4, which is consistent with the fact that girls in the
UCT arm who delayed marriage got quickly married following the end of the intervention. Striking
spikes in pregnancies and marriages in the UCT group immediately following the end of thetransfers are shown in Figure II. The temporary nature of the fertility changes in this group is also
reinforced by the fact that desired fertility remains unchanged (Table IV, Panel B, column 12).23
In analysis not shown in the tables, we find that teen pregnancy (defined as starting childbearing
at age 18 or younger) was significantly lower in the UCT arm at Round 3 (3.8 pp, p-value =0.027)
but that this effect had also shrunk by two thirds and was no longer significant by Round 4.
Beneficiaries of all ages experienced a spike in marriages and pregnancies following the program,meaning that UCTs reduced the prevalence of neither teen pregnancies nor child marriages byRound 4 – despite large reductions in these quantities at Round 3.

23

The finding of null effects in Round 4 in the UCT arm is not simply a function of lack of power. While the standard
errors of binary indicators for marriage and pregnancy are higher in Round 4 than in Round 3 due to the fact that thecontrol means for these variables are increasing towards 0.5 over the course of our study, minimum detectable effects
as a percentage of the mean in the control group are actually lower. Furthermore, these minimum detectable effects
are comparable to or lower than those presented in similar papers, such as Bandiera et al. (2017b). Finally, many of
the significant effects among baseline dropouts that we present in Table IV are larger than the minimum detectableeffects among baseline schoolgirls.

16Cash transfers can have effects on marriage and fertility via two channels. The firstpathway, apparent in the UCT arm, is through an income effect. In our study, this effect is strong
but disappears immediately when the transfers stop – as the transfers have not led to any
accumulation of physical or human capital. The other pathway, apparent in the CCT arm amongbaseline dropouts, is through increased schooling. Increased schooling is strongly associated withdelays in marriage and childbearing and reductions in desired and total fertility, but the impacts oftransfer programs on schooling need to be substantial to translate into meaningful and statisticallysignificant knock-on effects on marriage and fertility.

4.3 Health
Table V presents program impacts on biomarkers for HIV and anemia – the primary healthoutcomes specified in our pre-analysis plan. Program effects on HIV prevalence during the
program, i.e. at Round 2, were reported in Baird et al. (2012). Despite the improvements in
education, delays in marriage and fertility, and the high prevalence of HIV among baseline
dropouts (13.5% by Round 4), CCTs did not reduce HIV prevalence in this stratum at any point
during the study period (Panel A). Appendix Tables S4 and S5 examine self-reported sexual
behavior on the extensive and intensive margin. Both the onset of sexual activity and the likelihoodof being sexually active during the past year were lower among program beneficiaries during and
immediately after the program, but not two years later. There were no effects on risky sexual
behavior, such as having older partners or use of condoms, among those who reported being
sexually active. Nor did CCTs have significant effects on psychological wellbeing or nutritional
intake (Appendix Table S6).
Among baseline schoolgirls, program impacts on HIV mirror those on marriage andfertility over time: there is no effect of CCTs on HIV at Rounds 3 or 4, but a more than 50%
reduction in HIV prevalence in the UCT group (albeit, statistically significant only at the 90%
level) at the end of the intervention is no longer there two years later (Table V, Panel B). During
the two-year post-intervention period, which saw a spike in pregnancies and marriage in the UCTgroup, the incidence of HIV was 3.5 percentage points (pp) – compared with 2.0 pp in the control
group, though not statistically significant. Appendix Table S6 shows that effects of cash transfers
were equally transient on mental health and nutritional intake – strongly evident during the
program and disappearing afterwards. There is weak evidence of lower anemia prevalence in the17

UCT arm in Round 4, but this finding is not robust to either using a continuous measure ofhemoglobin levels, or to multiple hypothesis testing corrections presented in Section 4.5.

4.4 Labor Market Participation and Empowerment
The main activities performed by the baseline dropouts in our sample are household chores– such as cooking and cleaning, fetching water and firewood, and looking after children – (69.6%)
and subsistence agriculture (19.4%); among baseline schoolgirls, 55.2% report household chores
as their main activity, 11.1% report subsistence agriculture, while 27.5% are still in school. Hardly
anyone in our sample spent a significant amount of time in self-employment or paid work during
the past week (Table VI column 3), consistent with other data on labor market participation in
Zomba. Only a third of baseline dropouts and a quarter of baseline schoolgirls report having done
any wage work in the past three months (Appendix Table S7). There are no significant effects on
primary outcomes in either stratum, except a negative effect on typical wage among baseline
dropouts, which may reflect the fact that individuals in the treatment group were in school longer,
and thus might have less work experience. Program impacts on secondary labor market outcomes,
such as the effective daily wage, labor income in the past five seasons, and any wage work in thepast three months, are similarly null (Appendix Table S7).24
When we conduct exploratory analysis to investigate broader questions of time use, wefind that baseline dropouts in the treatment group are still spending more hours in school (1.54
hours per week, p=0.018), which may explain the negative effect on typical wage. When we lookat proportion of hours in school or work the impact is insignificant and zero (-0.001, p=0.930),
indicating that these additional hours in school are completely offset by additional hours in workby the control group. For baseline schoolgirls, we find that respondents in the CCT arm are
spending approximately 3.63 hours per week more in school (p=0.045) and that this does translate
to more time in work and school (2.4 percentage point more time in work or school, p=0.063). For
UCT recipients there are no impacts on either additional hours in school (-0.088, p=0.964) or timein work and school (0.001, p=0.919). This result supports the possibility of small positive sustained
impacts on time allocation for baseline schoolgirls in the CCT arm, with clear null effects in the
UCT arm.

24

We also examined accumulation of savings, household assets, and productive assets (such as livestock). We findno treatment effects on any of these outcomes in either stratum.

18

For baseline dropouts, program impacts on empowerment echo those on competencies,
health, and labor market participation: despite significant gains in educational attainment, delays
in marriage and pregnancy, and reductions in total live births, there are no effects on the overall
index of empowerment or subjective welfare (Table VI, Panel A, columns 4 & 5) and, in fact,
almost all coefficient estimates are negative. This finding holds when we examine empowerment
by marital status, i.e. on the intensive margin, at Round 4 (columns 6 & 7). Appendix Table S8shows estimates for the components of the female empowerment index (self-esteem, social
participation, preferences for child education, and aspirations).
For baseline schoolgirls in the CCT group, we also see no significant impacts on
empowerment or subjective wellbeing, although the coefficient estimates are generally positive.
However, in the UCT arm, the empowerment index is significantly lower than both the control andthe CCT groups (Table VI, Panel B). The -0.159 SD effect (p-value=0.05) on the super-index ofoverall empowerment among the UCT beneficiaries is reflected in the negative (but insignificant)effects in all sub-indices except aspirations (Appendix Table S8, Panel B), and is driven mainly
by a large (-0.342 SD; p-value<0.01) and significant negative association with empowerment
among those who are married (Table VI, Panel B, column 7). The findings indicate a statisticallysignificant divergence in female empowerment between CCT and UCT recipients among baselineschoolgirls two years after the end of the cash transfer program – particularly for those married by
Round 4, which may be related to the spike in marriages immediately after the cessation of cashtransfers (Figure II, Panel B).

4.5 Robustness of Findings to Attrition and Multiple Hypothesis Testing
Before we move on to analyzing child outcomes, we examine the robustness of program
impacts for the young women targeted by our cash transfer program. We address two concernswith our primary analysis: attrition and multiple hypothesis testing. First, in Section 3, we showedthat while the share of our study sample lost to follow-up more than four years after baseline datacollection is not high (between 12.5% and 15.7% in the control groups of the two strata), there isevidence of differential attrition in levels (but not characteristics) among baseline schoolgirls, andvice versa among baseline dropouts.25 We reiterate, however, that there is no differential attrition25

In addition, as mentioned above, a comparison of impact estimates in Rounds 2 & 3 using all the available data foreach of those rounds vs. the samples restricted to those available in Round 4 show qualitatively the same impacts.

19

in levels or characteristics between the CCT and UCT arms among baseline schoolgirls. As
differential attrition has the potential to bias impact estimates and, as such, is a threat to causal
inference, we conduct additional analysis to test the robustness of our findings. Second, as we
present impacts on 14 pre-specified primary outcomes in Round 4, we present q-values for impact
estimates that are adjusted for the false discovery rate (FDR) – to allay concerns that some of thestatistically significant impacts estimates might have materialized by chance.
In Appendix Tables S11-S13, we examine the potential effects that differential attrition
may have had on our results. In these tables, we present a central column (4) that re-states theimpacts shown earlier in the paper, using only sampling weights. In column (5), we estimate andimplement attrition propensity weights, first running a probit regression predicting presence in the
Round 4 sample with our standard battery of baseline covariates and their interaction withtreatment, and then weight outcomes by the product of the sampling weights and the inverse ofthis follow-up success probability. In columns (3) and (6) we present, respectively, the lower andupper bound estimates trimming the tails of the distribution following Lee (2009) to generate thesame observed attrition rates both treatment arms. In the remaining columns we follow Kling and
Liebman (2004) and impute to the missing observations the mean within that treatment arm plus
or minus 0.1 * the arm-specific standard deviation (columns (2) and (7)) and plus or minus 0.25 *the standard deviation (columns (1) and (8)). For the lower bounds this amount is subtracted fromthe treatment and added to the control, and for the upper bounds this is reversed.
For baseline dropouts, we note that the Lee bounds are tight around the original estimate
because the difference in the level of attrition between the control and the CCT groups is verysmall (Appendix Table S11). Furthermore, IPW-adjusted impact estimates are very close to our
original estimates. Even the Kling and Liebman bounds present a very consistent picture of
impacts; across the full set of bounds we find significant impacts of the CCT on highest grade
completed, ever married, and number of live births. Nothing in the table suggests that we should
significantly revise our interpretation of the key findings of program impacts among baseline
dropouts. Similarly, for baseline schoolgirls, IPW-adjusted estimates are nearly indistinguishable
from the original estimates, while the Lee bounds are wider because of the larger difference inattrition levels between the control group and either treatment group (Appendix Table S12). For
baseline schoolgirls there are no outcomes that are significant across bounding strategies, although
the negative effects of unconditional treatment on empowerment and anemia come close. These

20

wider bounds mean that while our original and IPW-adjusted estimates generally indicate a lackof impact of CCTs or UCTs among baseline schoolgirls in Round 4, we cannot rule out sizeable(positive) impacts for some of the more intermediate outcomes, such as highest grade completed
and competencies.
Finally, Appendix Table S13 shows that pairwise comparisons of CCT and UCT impacts
are completely robust to the adjustments we implement, which confirm that (a) most of thestatistically significant differences in schooling, marriage, and fertility that existed between these
two treatment arms immediately after the program disappeared two years later, and (b) UCT
beneficiaries have a lower level of overall empowerment than CCT beneficiaries by Round 4.
In summary, the analysis above confirms that our medium-term impact findings amongbaseline dropouts and the comparison of relative impacts of CCTs vs. UCTs among baselineschoolgirls are strongly robust to alternative means of handling attrition in the data. On the other
hand, for comparisons of CCTs or UCTs with the pure control group among baseline schoolgirls,
it is prudent to allow for the possibility of positive impacts on education and health and negative
effects on labor market participation (perhaps due to higher likelihood of being in school).
In Table VII, we present q-values controlling for FDR, as described in Anderson (2008).
We use Anderson’s Stata code to calculate FDR-adjusted q-values, which uses a simple method
proposed by Benjamini and Hochberg (1995) to calculate the smallest q at which each hypothesis
would be rejected.26 The q-values for the 14 primary outcomes in this study are calculated
separately for each key comparison: CCT vs. Control among baseline dropouts; and then CCT vs.
Control, UCT vs. Control, and CCT vs. UCT among baseline schoolgirls. These estimates,
presented alongside the original p-values of the impact estimates for each treatment arm, confirm
the robustness of our findings to multiple hypothesis testing adjustments: every statisticallysignificant impact for the CCT arm among baseline dropouts has a q-value below 0.099, while
every q-value is greater than 0.289 among baseline schoolgirls.
Our analysis so far points to two main findings: first, among the more vulnerable group of
baseline dropouts, CCTs improved school attainment and decreased marriage and fertility rates,
which were sustained over time. Second, the large effects of UCTs among baseline schoolgirls

26

The Stata code and the paper that describes the method can be found here:
https://are.berkeley.edu/~mlanderson/ARE_Website/Research.html.

21during the program have all but disappeared within two years. In this sub-section, we found thatthese two main findings are robust to attrition and multiple hypothesis testing.
4.6 Child Outcomes
We conclude this section with a discussion of program impacts on children born to study
participants. Policies for child development often target the first 1,000 days – from conception to
the second birthday (Barham, Macours and Maluccio 2013), a period during which improvements
in family income may be particularly important for children’s development.27 In our experiment,
more than 2,000 babies were born to study participants by Round 4 – with endogenous variationin their duration of exposure to the cash transfer program. We have already demonstrated that wellknown channels for growth, such as maternal nutrition and stress (Black, Devereux and Salvanes2016), improved during the two-year program.
In terms of the timing and structure of the cash transfers, we would expect substantial
heterogeneity of program impacts on child outcomes both by when the birth took place andwhether the transfers to the mother were conditional on school attendance. As in other countries
in the region, childbearing and schooling are mutually exclusive in Malawi (Baird, McIntosh andÖzler 2011; Ozier 2015), meaning that the condition to regularly attend school effectively screensout most expecting and new mothers in the CCT arm: only in the UCT arm would mothers withnewborn children continue receiving transfers. Secondly, even in the UCT arm, a child conceived
after the end of the program would have had no direct exposure to the program and, as we haveshown earlier, the average mother would have acquired no additional education that could provide
subsequent human capital-driven benefits. On the other hand, increased mother’s education can,for example, increase child height (Thomas, Strauss and Henriques 1991), so we might expect tosee benefits among children born after the program in the CCT groups – particularly amongbaseline dropouts, who experienced large gains in school attainment themselves. These causal
chains suggest that UCT benefits should be concentrated among children born or in utero during

27

Agüero, Carter and Woolard (2006) study the effect of Child Support Grants in South Africa for children who were
exposed to the program up to three years after birth and find sizeable effects of increased exposure to these
unconditional cash transfers on child height. Milligan and Stabile (2009), studying child benefits in Canada, findeffects on cognitive and socio-emotional skills of children aged 4-6. Dahl and Lochner (2012) using the variation in
Earned Income Tax Credit in the U.S., find that increased income improves children’s test scores. Currie and Almond(2011) review the effects of “near cash” programs, such as food stamps, in the U.S. and find credible evidence ofeffects on birth weight. Finally, Aizer et al. (2016) and Hoynes, Schanzenbach and Almond (2016) find that children
whose parents received cash transfers and food stamps in the U.S. had improved education, health, and income asadults.

22

the program, while CCTs might be most beneficial to children born after the mother’s additional
human capital accumulation took place.28
Since the program caused significant changes in fertility patterns (Table IV), the raw
treatment-control differences in, say, height are not interpretable as causal impacts of the programon a specific child, because childbearing is endogenous to treatment. To address this, we pursue
two approaches: estimation of heterogeneity by child age, and regression/reweighting control for
selection-driven covariates. The technical details of the assumptions that are required for thisapproach and the sequence of adjustments that we made are outlined in Appendix A. We
concentrate our analysis on height-for-age z-scores (HAZ), which is an objectively measured
indicator of stunting that affects almost 50% of children under the age of five in Malawi, and is astrong predictor of productivity as an adult in low income settings (LaFave and Thomas 2016).29
First, we can examine how treatment effects vary across three ‘epochs’ defined by childage. The first epoch captures those directly exposed to the program, meaning those born during
the program.30 The second epoch covers those born within nine months of the end of the program,
who were exposed in utero for a maximum of nine months. Finally, the third epoch covers thoseborn more than nine months after the end of the program, who were not exposed to cash transfers
either as children or in utero and could only benefit from the program due to improved outcomesof their mothers.
Figure III plots the “raw” differences in HAZ for children under 60 months between thetreatment and the control groups (the thinner curves in plain font).31 The figures are consistent
with the hypothesis that differences in children’s heights are moderated by exposure to the28

Increased age at first birth can also have positive effects on child height through improved gynecological maturity
and decreased competition for nutrition between the mother and the child in utero, which could operate in any
treatment group that delayed pregnancies.
29
Of the two anthropometric measures that we collected for children aged 0-59 months – height and weight – stunting(height-for-age z-score<-2) is the key indicator of malnutrition in Malawi: almost half of the children under the ageof 5 were categorized as stunted in 2010, while wasting (weight-for-height z-score<-2) rates are low at 4% (IFPRI
2014). Child assessments are also objectively measured outcomes of cognitive and socio-emotional development, but
the target age group for the assessments that we chose for this study (36-59 months) makes them unsuitable for analysis
by epoch of exposure to the program because only children born during the first year of the program (less than 200 in
the baseline schoolgirl stratum with less than 30 in the UCT arm) were eligible for assessment.
30
The percentage of baseline schoolgirls who reported having been ever pregnant was less than 2% at baseline. Hence,children directly exposed to the program in this stratum are almost exclusively born during the intervention. However,approximately 45% of baseline dropouts had already started childbearing at baseline. Therefore, our analysis includes
children under two at the start of the program, who were at least partially exposed to cash transfers.
31
We construct these figures by running a locally weighted treatment effects regression across the distribution of childage (Fan 1992) and plotting the resulting time-specific treatment effects and 95% confidence intervals. The figuresplot robust standard errors clustered at the EA level, as in the main regressions.

23

program. Most strikingly, we see a very large difference in HAZ between the UCT and the control
group during the program, which steadily declines, disappears by the end of the program, and eventurns negative during the final epoch (Panel C). This pattern is consistent with the substantive buttransient improvements in the nutritional status and mental health of UCT beneficiaries. In
contrast, no significant differences in child height are apparent between the CCT and the control
groups during the program – also consistent with the fact that most mothers of children born inthis period would have dropped out of school because of their pregnancies, thus forgoing any cashtransfers (Panels A and B). Column 1 in Tables VIII and IX reports the raw differences in HAZ
by epoch, for baseline dropouts and baseline schoolgirls respectively, and confirms these patterns.
Next, we attempt to control for endogenous selection via propensity weighting andregression control. The treatment/control comparisons may combine extensive margin selection
effects (such as the types of women who became pregnant, the types of partners they chose, andthe age at birth) with a ‘direct’ casual effect of the program on the identities of the children
observed in the Round 4 sample. Unlike many such applications in the natural experimental
literature, it is entirely plausible that all of the observed impacts on HAZ arise from the selection
effect of unwanted children being delayed by the receipt of the UCT.32 Following the methodology
laid out in Appendix A, we can then sequentially implement a set of selection controls: in Column
2 we use a set of baseline maternal characteristics to predict fertility in each epoch, and include
inverse propensity weights based on fertility probabilities in the analysis (as well as including thesecovariates in the regression) to provide estimates of impact that are doubly robust to maternal typeselection. Column 3 includes covariates controlling for paternal type, Column 4 adds flexible
controls for child age, while Column 5 adds indicator variables for the mother’s age at birth andinteractions of maternal age with all other baseline covariates. Subject to the assumptions laid out
in Appendix A, these estimates allow us to move from the reduced-form ‘raw’ treatment effects toestimates of a ‘direct’ effect – i.e. suggestive ceteris paribus impacts of CCTs and UCTs on thechildren born in each epoch.

32

In the study of a negative shock, the most likely extensive margin impact is an increase in mortality among theweakest fetuses and children, hence pushing upwards the average outcome among surviving cohorts exposed to theshock. The large set of papers studying negative shocks such as pollution (Chay and Greenstone 2003; Adhvaryu etal. 2016; Black et al. 2017), disease (Almond 2006), and hunger (Almond and Mazumder 2011) can typically argue
that any negative effects found on surviving children are conservative. Because we study a positive shock that may
have delayed pregnancies with worse expected outcomes, the selection and direct treatment effects in our case may
both point to superior child outcomes in the treatment condition. Decomposing these effects is therefore critical.

24

Column 2 in Table IX, Panel A shows that the maternal selection controls alone reduce theeffect of UCTs during the program by almost a half (from .953 to .525 SD), confirming significant
positive selection into childbearing during the program in the UCT arm. The other pathways havea limited effect, resulting in a fully adjusted direct effect of .523 SD (column 5). The size of thisremaining direct effect is consistent with Barham, Macours and Maluccio (2013), who report thatchildren in Nicaragua who received three years of cash transfers were 0.2-0.4 SD taller; and with
Agüero, Carter and Woolard (2006), who find that children in South Africa receiving child support
grants for most of the period between 0-3 years of age gained as much as 0.45 SD in HAZ.33 The
bold curves in Figure III plot these ‘direct’, fully adjusted Fan regressions across the month ofbirth, including the battery of controls included in Column 5 of Tables VIII & IX. The distributionof direct treatment effects in the UCT arm shown in Panel C is remarkably consistent with what
we would expect: a significant and positive effect on HAZ among children born during the
program, which disappears immediately following the cessation of transfers.34
The effects on HAZ in the CCT groups are also as expected: as females who dropped outof school due to pregnancies did not continue to receive transfers, we would expect little effect on
their children born during the program. Conversely, if increased education or delaying
childbearing influences child height, we might see effects among children of CCT recipients bornafter the program. Among baseline dropouts or baseline schoolgirls, we see no significant effects
on HAZ for babies born during the program. However, the corrected tables show modest (0.100.25 SD), but statistically non-significant, improvements in HAZ for children born after the
program to baseline schoolgirls who received CCTs (Table IX, Panels A & C, column 5).
The findings here are consistent with the theory that underlies the tradeoff between CCTs
for schooling and UCTs: UCTs primarily confer an income effect on children born during the
program and no effects on children born later because they do not lead to an accumulation ofcapital (human, physical, or social) for the mother.35 On the other hand, CCTs deny such benefits
33

Examining an ongoing CCT program in Indonesia, Cahyadi et al. (2018) find reductions of 23 to 27 percent in theprobability of being stunted (and 56 to 62 percent in the probability of being severely stunted) among children aged
0-5 six years after the start of the program.
34
If there is a pure income effect on child height, it is possible that this effect responds to increased transfer amounts.
In Appendix Table S14, we investigate the effect of randomly assigned transfers to the core respondent and herhousehold separately. These estimates provide suggestive evidence of decreased psychological distress and increased
consumption of meals with animal proteins as a function of unconditional transfer amounts to the core respondent.
35
We do not see any positive effects of UCTs for babies born within nine months from the end of the program, i.e.
those exposed in utero. While this may be considered surprising given the extant evidence on the importance of thisperiod for physical development, it should be remembered that the young mothers are also dealing with the cessation25

to the children of non-compliers during the program, but may have modest effects on futurechildren through increased human capital accumulation.

5. CONCLUSION
The most striking feature of the findings presented in this paper is the transience of the
impact of unconditional cash transfers. Particularly glaring are the fleeting decreases in childmarriage and teen pregnancy in the UCT arm, along with psychological distress and HIV – theprevalence of all of which reverted to control group levels within just two years, implying
significant but temporary income effects. Within months of the end of the program, many UCT
beneficiaries became pregnant, and were married soon thereafter.
On the other hand, there were sustained program effects on school attainment, earlymarriage, and pregnancy for baseline dropouts receiving CCTs. However, these effects did nottranslate into reductions in HIV, gains in labor market outcomes, or increased empowerment.36
Several reasons might explain the disconnect between increased school attainment and no
improvements in labor market outcomes, empowerment, or health. First, it is possible that
increased schooling does not provide one with the skills needed to increase future welfare in thiscontext. There are very few formal sector jobs for women in Malawi and most households depend
on subsistence farming and a variety of informal sector activities. We administered tests of skills
needed in farming and running small household enterprises and detected no effects in these
domains. If safe and well-paying jobs existed for women in Malawi, households might invest in
the necessary human capital of adolescent females on their own – perhaps even without the helpof any outside interventions (Munshi and Rosenzweig 2006; Jensen 2012; Oster and Steinberg
2013; Heath and Mobarak 2015). Second, task performance is dependent on not only
improvements in cognitive skills, but also on character skills and effort (Heckman and Kautz
2013). Hence, it is possible that CCTs, by providing incentives for formal schooling, improved
only cognitive skills, which may not have been enough to increase productivity.37
of support during this same period. Changes in lifestyle and increased stress from the loss of regular income during
this transitional period may have dampened any beneficial effects of cash transfers on the child in utero.
36
The findings on marriage, pregnancy, and HIV are consistent with Duflo, Dupas and Kremer (2015), who find that
education subsidies in Kenya reduce dropout, pregnancy, and marriage, but not sexually transmitted infections. Theysuggest a model in which choices between committed and casual relationships, rather than unprotected sex alone,affect pregnancy and HIV.
37
Heckman and Mosso (2014) state “The most effective adolescent interventions target formation of personality,
socioemotional, and character skills through mentoring and guidance, including providing information.” Bandiera et26

Our study provides some important guideposts for the design of effective adolescentfocused cash transfer programs. First, the palliative benefits of small and frequent unconditional
cash transfers are uncontested and reinforced by our study, but the idea that they can contribute toa sustained improvement in welfare over the longer-run is unproven and not supported here.38
Second, we shed further light on the tradeoffs between the benefits of conditional andunconditional transfers. The lack of knock-on effects from schooling gains in this context implies
that the imperative to use conditions to generate increased investments in human capital may be
weak when few income-generating opportunities exist. Moreover, by denying noncompliant
adolescent girls and young women cash transfers at precisely the moment when they are most
likely to start childbearing, a myriad of potential benefits is missed under CCT programs.
A potentially promising way of resolving this tradeoff is to view CCT and UCT programs
as complements to each other rather than alternatives: policymakers could provide a basic
unconditional cash transfer to adolescent girls topped up by conditional cash transfers for humancapital accumulation and desired health behaviors – providing both an incentive to invest in
education and health while still guaranteeing a basic level of protection to those who are unable orunwilling to comply with the conditions. Third, and finally, the promising (if only suggestive)
evidence of the positive effect of UCTs on children’s height provides an additional reason toconsider providing basic UCTs to adolescent females. Indeed, Currie and Almond (2011) havesuggested that targeting transfers towards women of childbearing age may be beneficial in the U.S.
context, so as to maximize benefits to children in utero. This form of targeting would suffer fromremarkably little ‘leakage’ in the Malawian context; two thirds of women aged 20-24 gave birthby age 20 and virtually all females have started childbearing by age 25 (National Statistical Officeand ICF Macro 2005).
Our study has some limitations. First, differential attrition levels between either treatment
arm and the control group among baseline schoolgirls reduces the precision of and the confidence
in the null impact estimates in Round 4. Second, we examine the height of children born to study
participants, which itself is endogenous to treatment. Therefore, the non-experimental impactal. (2017b) provide suggestive evidence that a mentoring program in Uganda (ELA) that provided young females with“hard” vocational and “soft” life skills may have led to longer-term improvements in welfare.
38
We do not mean to downplay or underestimate the effects of redistributive policies on current poverty and inequality
reduction, even if they do not lead to substantive increases in human capital accumulation among adolescents. Welfare
gains from such effects can be as large as, if not larger than, those from human capital investments (Alderman,
Behrman and Tasneem 2015).

27

estimates on HAZ should be treated as suggestive. Finally, the study sample of initially nevermarried females, aged 13-22 had not yet completed their transition from adolescence to adulthoodby Round 4, especially in the baseline schoolgirl stratum. Hence, it is important to allow for the
possibility that clearer program impacts may emerge in a future round of data collection on
important outcomes such as skills, labor market participation, earnings, and empowerment.
Given the medium-term nature of these results, it is natural to ask how much we can infer
about longer-run impacts. As our study captures outcomes a little more than two years after the
cash transfers stopped, we cannot speak to long-term effects, such as those analyzed in the U.S.
context in recent studies (Aizer et al. 2016; Hoynes, Schanzenbach and Almond 2016). To guideour thinking, we return again to the role of productive assets in generating long-term rewards: tomake an impact later in life, a program must have meaningfully shifted the stock of some form ofcapital that can generate returns over the long haul. For baseline dropouts, who were offered CCTs
to return to school, the increase in school attainment, and the subsequent drop in fertility, issizeable. For this group, it may be premature to conclude that improvements in education will leadto no long-term gains. If the relationship between education and wages becomes steeper with age,or if household-level human capital alters the economic trajectory of these households, future
follow-up studies may well reveal longer-term benefits. For baseline schoolgirls in the UCT arm,
our findings suggest that two years of financial support during adolescence might have been too
short – rather than a two-year follow-up window being too short to trace out subsequent impacts.39
Only two years after the end of the program, UCT beneficiaries are, in most respects, in a positionindistinguishable from where they would have been in the absence of cash transfers. The
unwinding of the program impacts on marriage and pregnancy is immediate and substantial, so,given the lack of school attainment or learning effects in this group, it is only their children inwhom we note some vehicle for durable improvements in human capital.

However, it should be noted that the Mothers’ Pension program of the early 20th century U.S. had a median durationof three years and was of similar generosity to many cash transfer programs today (Aizer et al. 2016), including ours,
and showed long-term effects in health, education, and income among children of program beneficiaries.
39

28

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34

Urban Household
Mother Alive
Father Alive
Household Size
Asset Index
Age
Highest Grade Attended
Never Had Sex
Ever Pregnant
Chi-squared joint test oforthogonality (p-value)

Table I: Baseline means and balanceBaseline Dropout
Baseline Schoolgirl
Mean (s.d.)Mean (s.d.)
Conditional
Control Conditional Unconditional
Control group
group
group
group
Group
(1)
(2)
(3)
(4)
(5)
0.181
0.129
0.346
0.478
0.418
(0.385)(0.335)(0.476)(0.500)(0.494)
0.783
0.749
0.839
0.800
0.828
(0.413)(0.434)(0.368)(0.401)(0.378)
0.656
0.649
0.709
0.718
0.76
(0.476)(0.478)(0.454)(0.451)(0.428)
6.120
6.104
6.375
6.341
6.659
(2.388)(2.617)(2.262)(2.134)(2.063)-0.831-0.7430.632
1.100
1.373*(2.233)(2.484)(2.575)(2.721)(2.444)17.57917.16215.22814.91915.466(2.397)(2.478)(1.904)(1.828)(1.926)
6.105
5.940
7.506
7.262
7.928**(2.856)(2.864)(1.651)(1.601)(1.587)
0.315
0.294
0.800
0.807
0.790
(0.465)(0.456)(0.400)(0.395)(0.408)
0.445
0.420
0.021
0.029
0.029
(0.498)(0.494)(0.144)(0.169)(0.168)
0.168

0.122

0.121

p-value(CCTUCT)
(6)
0.726
0.431
0.341
0.156
0.572
0.002
0.004
0.682
0.964
0.032

Notes: Mean differences statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence. Stars on thecoefficients in columns (2) indicate significantly different than the control group for baseline dropouts.Stars on the coefficientsin column (4) and (5) indicate significantly different than the control group for baseline schoolgirls. Means are weighted to makethem representative of the target population in the study EAs.

Table II: Attrition
Baseline Dropout(1)=1 if Conditional=1 if Completed Household Survey Round 4
(2)
(3)

(4)

-0.007(0.031)-0.008(0.029)0.055***(0.019)0.058***(0.023)0.056***(0.018)0.061***(0.021)

0.828

0.774

0.896
0.004

0.825
0.002

NO

YES

NO

YES

-

0.009

-

0.332

-

-

-

0.101

-

-

-

0.690

0.843
885

0.843
885

0.875
2,273

0.875
2,273

=1 if Unconditional
p-value UCT vs. CCT
p-value Treatment
Baseline controls interactedwith treatment?
p-value on joint F-test forinteractions CCT
p-value on joint F-test forinteractions UCT
p-value UCT interactions vs.
CCT interactions
Mean in Control Group
Number of observations

Baseline Schoolgirl

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions areweighted to make them representative of the target population in the study EAs. All regressions include baseline
centered values of the following variables: age indicators, stratum indicators, household asset index, highest grade
attended, an indicator for never had sex. Columns (2) and (4) interact the centered baseline controls with treatment.
Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

36

Table III: Program impacts on education and learning (beneficiaries)
Panel A: Baseline Dropouts

DuringEnd ofTwo Years
Program Program After Program
(1)
(2)
(3)
0.579*** 0.558***
0.621***(0.073)(0.102)(0.125)
6.345
6.967
6.997
697
718
744

(4)
0.079
(0.071)
0.000
704

(5)
0.147***(0.056)
0.000
704

(6)
0.116
(0.072)
0.000
704

(7)
0.163**(0.070)0.000
704Competencies
Score(Standardized)
Two Years
After Program
(8)
0.064
(0.057)
0.000
742

0.078
(0.090)0.122(0.109)
0.708
0.469
8.590
1,965

0.148***(0.056)-0.068(0.090)
0.035
0.021
0.000
2,000

0.136**(0.069)-0.027(0.106)
0.157
0.118
0.000
2,000

0.068
(0.063)0.026(0.090)
0.657
0.560
0.000
2,000

0.181***(0.050)0.094(0.129)
0.514
0.002
0.000
2,000

0.065
(0.058)0.098(0.067)
0.630
0.297
0.000
2,048

Highest Grade Completed=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size
Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample Size

0.126*(0.069)0.103(0.121)
0.854
0.174
9.677
2,019

0.120
(0.080)0.095(0.129)0.850
0.309
10.415
2,049

English Test TIMMS Math Non-TIMMS
Score
Math Score
Score(Standardized) (Standardized) (Standardized)

Cognitive Test
Score
(Standardized)

End of Program

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to make them representative of the target population in
the study EAs. The cognitive test score is based on Raven’s Colored Progressive Matrices. Math and English reading comprehension tests were developed based on the
Malawian school curricula. Five questions (four from the Fourth Grade test and one from the Eighth Grade test) from Trends in Mathematics and Science Study (TIMMS)
2007, which is a cycle of internationally comparative assessments in mathematics and science carried out at the fourth and eighth grades every four years, were added to themath test. Competencies represent a set of skills that were anticipated to be sensitive to education and relevant for non-formal employment. The skills tested included reading
and following instructions to apply fertilizer; making correct change during hypothetical market transactions; sending text messages and using the calculator on a mobile
phone, and calculating profits under hypothetical business scenarios. All test scores and the competency index were standardized to have a mean of zero and a standard
deviation of one in the control group. Baseline values of the following variables are included as controls in the regression analyses: age indicators, stratum indicators,
household asset index, highest grade attended, an indicator for never had sex, and whether the respondent participa+A1:I29ted in the pilot phase of the development of thetesting instruments. We restrict the sample to respondents who were surveyed during the latest household survey conducted two years after the program (Round 4). Note thatin Rounds 2 and 3, highest grade completed is actually highest grade attended. Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*)
confidence.

Table IV: Program impacts on marriage and fertility (beneficiaries)
Panel A: Baseline Dropouts=1 if Ever Married

Mean in Control Group
Sample Size
Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample Size

=1 if Ever Pregnant

Number of Live Births

Age at First
Birth

DesiredFertility

End of
ProgramTwo Years
After
ProgramTwo Years
After
ProgramDuring
Program

End ofTwo Years
During End of
Program After Program Program Program

Two Years
After
ProgramTwo Years
After
ProgramTwo Years
After
Program(1)(2)-0.140*** -0.157***(0.029)(0.037)
0.291
0.575
698
718

(3)
-0.107***(0.032)
0.809
744

(4)
0.431***(0.155)19.644500(5)-0.057*(0.030)
0.610
698

(6)
-0.081***(0.027)
0.784
718

(7)
-0.040*(0.021)
0.924
744

(8)
(9)
-0.005 -0.095**(0.033) (0.044)
0.520
0.819
698
718

(10)
-0.147***(0.054)
1.380
744

(11)
0.272*(0.164)18.499634(12)-0.172*(0.087)
3.217
744

0.000
-0.010(0.012)(0.024)-0.033*** -0.083***(0.012)(0.024)
0.026
0.018
0.023
0.004
0.047
0.180
1,967
2,018

-0.035(0.027)-0.010(0.046)
0.613
0.448
0.402
2,049

-0.011(0.148)0.486**(0.200)0.032
0.050
18.651821

0.008(0.015)-0.013(0.017)
0.314
0.600
0.092
1,966

0.027
(0.027)-0.063**(0.028)
0.009
0.025
0.247
2,019

-0.024(0.034)-0.001(0.042)
0.614
0.760
0.501
2,049

0.023*(0.014)0.013(0.017)
0.641
0.209
0.055
1,966

0.020
(0.036)-0.024(0.046)
0.410
0.705
0.511
2,049

-0.144(0.136)0.001(0.168)0.436
0.547
18.718998-0.072(0.064)-0.017(0.056)
0.477
0.533
2.974
2,048

During
Program=1 if Conditional Schoolgirl

Age First
Marriage

0.003(0.022)-0.055*(0.030)
0.075
0.151
0.199
2,019

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. We correct for inconsistencies in 'ever married' and 'ever pregnant' across rounds.All regressions are weighted tomake them representative of the target population in the study EAs. Baseline values of the following variables are included as controls in the regression analyses: age indicators, stratum indicators,
household asset index, highest grade attended, and an indicator for never had sex. We restrict the sample to respondents who were surveyed during the latest household survey conducted two years after the
program (Round 4). Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

38

Table V: Program impacts on HIV and Anemia (beneficiaries)
Panel A: Baseline Dropouts

(2)
0.020
(0.023)

Two
Years
After
Program(3)
0.012(0.026)=1 if
Anemic
Two
Years
After
Program(4)
0.039(0.035)

0.06
373

0.094
694

0.135
715

0.255
711

-0.020**(0.009)-0.015(0.012)
0.616
0.112
0.026
1,192

-0.003(0.011)-0.019*(0.012)
0.237
0.249
0.035
2,002

-0.001(0.019)-0.002(0.023)
0.980
0.996
0.055
1,977

0.012
(0.031)-0.065*(0.033)=1 if HIV Positive=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size
Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample SizeDuring
Program

End of
Program(1)
0.022(0.024)

0.068
0.122
0.243
1,979

Notes: Regressions are OLS models with robust standard errors clustered at the EA level.
All regressions are weighted to make them representative of the target population in the
study EAs. An individual is considered anemic if her hemoglobin count is less than or equal
to 11g/dL if pregnant and less than or equal to 12d/dL if non-pregnant based on WHO
guidelines to define mild anemia. Baseline values of the following variables are included ascontrols in the regression analyses: age indicators, stratum indicators, household asset index,
highest grade attended, and an indicator for never had sex. We restrict the sample torespondents who were surveyed during the latest household survey conducted two years
after the program (Round 4). Parameter estimates statistically different than zero at 99%(***), 95% (**), and 90% (*) confidence.

Table VI: Program impacts on labor market outcomes and empowerment (beneficiaries: primary outcomes)
Panel A: Baseline Dropouts
Labor Market Outcomes

Empowerment

Proportion of
Change in
Typical Wage Hours Spent Super-Index ofSuper-Index ofOpportunity
Subjective
in Past Threein SelfOverall
Unmarried
Cost of Time
Wellbeing fromMonthsEmployment Empowerment
Empowerment(2012 USD)
Five Years Ago(2012 USD) or Paid Work (Standardized)(Standardized)
to Todayin Past Week

Super-Index of Married Index
Marriedof Economic
Empowerment
Control(Standardized) (Standardized)

Two Years After Program=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size
Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample Size

(1)-0.037(0.079)
0.707
718

(2)
-0.140**(0.068)
0.375
743

(3)
-0.011(0.009)
0.061
744

(4)
-0.083(0.074)
0.000
744

(5)
-0.032(0.232)
1.120
744

(6)
0.018
(0.112)
0.000
289

(7)
-0.113(0.102)
0.000
455

(8)
-0.118(0.096)0.000
455-0.051(0.101)-0.115(0.074)
0.550
0.297
0.897
2,002

-0.011(0.058)0.036(0.104)
0.665
0.910
0.212
2,048

0.003
(0.005)0.002(0.008)
0.842
0.784
0.029
2,045

0.049
(0.082)-0.159*(0.081)
0.052
0.101
0.000
2,049

0.276
(0.187)0.176(0.190)
0.650
0.306
0.906
2,049

0.111
(0.098)-0.094(0.109)
0.120
0.287
0.000
1,271

0.068
(0.095)-0.342***(0.099)
0.001
0.001
0.000
776

-0.107(0.108)0.147(0.307)
0.406
0.484
0.000
774

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to make them representative of the target population in the
study EAs. Opportunity cost of time is calculated by taking the minimum daily wage the respondent would take for one year of work in her village. Detail on the construction of thesuper-indices can be found at https://drive.google.com/file/d/1hvI79ltywocFr-pafqz8_Dtg2ZXNhcHd/view. The change in subjective wellbeing asks the respondent where she sees
herself on a 10-step ladder comparing five years ago to today, where zero represents the worst possible life she could have and 10 represents the best possible life she could have.
Baseline values of the following variables are included as controls in the regression analyses: age indicators, stratum indicators, household asset index, highest grade attended, and an
indicator for never had sex. We restrict the sample to respondents who were surveyed during the latest household survey conducted two years after the program (Round 4).
Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

Table VII: Primary outcomes with multiple testing adjustments (original p-values and FDR q-values)
Baseline Schoolgirl
Outcomes

Highest Grade CompletedCompetencies Score (Standardized)=1 if Ever Married
Age at First Marriage=1 if Ever Pregnant
Number of Live Births
Age at First Birth= if HIV Positive=1 if Anemic
Opportunity Cost of Time
Typical Daily Wage in Last Three
Months
Proportion of Hours Spent in SelfEmployment or Paid Work in Past
Super Index of Overall
Empowerment (Standardized)
Change in Subjective Wellbeingfrom Five Years Ago to Today

Baseline Dropout

CCT vs. Control

UCT vs. Control

CCT vs. UCT

CCT vs. Control(1)p-value(2)
q-value(3)
p-value(4)
q-value(5)
p-value(6)
q-value(7)
p-value(8)
q-value

0.136

1.000

0.465

1.000

0.850

1.000

0.000

0.007

0.269

1.000

0.147

0.478

0.630

1.000

0.263

0.237

0.206

1.000

0.829

1.000

0.613

1.000

0.001

0.007

0.940

1.000

0.016

0.289

0.032

0.465

0.006

0.022

0.471

1.000

0.980

1.000

0.614

1.000

0.054

0.099

0.580

1.000

0.600

1.000

0.410

1.000

0.007

0.022

0.292

1.000

0.997

1.000

0.436

1.000

0.100

0.145

0.955

1.000

0.938

1.000

0.980

1.000

0.649

0.504

0.699

1.000

0.053

0.299

0.068

0.465

0.263

0.237

0.617

1.000

0.120

0.478

0.550

1.000

0.641

0.504

0.847

1.000

0.726

1.000

0.665

1.000

0.041

0.090

0.502

1.000

0.831

1.000

0.842

1.000

0.221

0.237

0.551

1.000

0.051

0.299

0.052

0.465

0.890

0.504

0.143

1.000

0.354

1.000

0.650

1.000

0.263

0.237

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to make them
representative of the target population in the study EAs. Baseline values of the following variables are included as controls in the
regression analyses: age indicators, stratum indicators, household asset index, highest grade attended, an indicator for never had sex, andwhether the respondent participated in the pilot phase of the development of the testing instruments. We restrict the sample torespondents who were surveyed during the latest household survey conducted two years after the program (Round 4). Parameter estimates
statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

Table VIII: Program impacts on height-for-age z-scores (children of beneficiaries: baseline dropouts)
Raw EffectDirect Effect+ Maternal+ Paternal+ Mother
Panel A: Born During Program
Gender
Selection
Selection+ Child Age
Ageweights
Controls
(1)
(2)
(3)
(4)
(5)
=1 if Conditional Schoolgirl-0.015-0.174-0.139-0.154-0.051(0.128)(0.149)(0.143)(0.140)(0.136)
Sample Size
367
367
367
367
367
Panel B: Born Within 9 Months of Program Ended=1 if Conditional Schoolgirl
0.353
0.518*
0.394
0.411*
0.577**(0.296)(0.303)(0.249)(0.234)(0.260)Sample Size
88
88
88
88
88
Panel C: Born More than 9 Months After Program Ended=1 if Conditional Schoolgirl-0.269-0.175-0.127-0.137-0.183(0.168)(0.192)(0.161)(0.154)(0.152)
Sample Size
287
287
287
287
287
Control Structure:
Maternal selection controls + propensity weight
X
X
X
X
Father selection controls
X
X
X
Cubic in child age in months
X
X
Maternal age in years, age interactions
X
Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to makethem representative of the target population in the study EAs. The height-for-age z-score is calculated using the 2006 WHO child
growth standards. Specification (1) controls for the gender of the child. Specification (2) adds selection weights and controls
directly for maternal baseline characteristics ( stratum indicators, household asset index, highest grade attended, and an indicator fornever had sex). Specification (3) adds controls for paternal attributes (highest education level, religion, ethnicity, main activity, andlikely HIV status). Specification (4) adds a linear, quadratic, and cubic in child age. Specification (5) adds maternal age andmaternal age interacted with the other baseline covariates. We restrict the sample to respondents who were surveyed during thelatest household survey conducted two years after the program (Round 4). Parameter estimates statistically different than zero at
99% (***), 95% (**), and 90% (*) confidence.

Table IX: Program impacts on height-for-age z-scores (children of beneficiaries: baseline schoolgirls)
Raw EffectPanel A: Born During Program=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Sample Size

Direct Effect

Gender+ Maternal
Selectionweights+ Paternal
Selection
Controls+ Child Age+ Mother
Age

(1)
0.155
(0.162)
0.953**(0.476)
0.091
0.123
315

(2)
-0.050(0.192)0.525**(0.221)
0.022
0.040
315

(3)
-0.054(0.186)
0.549*(0.306)
0.028
0.089
315

(4)
0.023
(0.177)
0.666**(0.315)
0.024
0.072
315

(5)
0.124
(0.155)0.523*(0.299)
0.115
0.218
315

0.156
(0.263)0.163(0.315)
0.984
0.787
211

0.235
(0.240)0.109(0.336)
0.725
0.619
211

0.125
(0.175)-0.431**(0.183)
0.013
0.028
211

0.086
(0.194)-0.434**(0.193)
0.028
0.047
211

0.497
(0.445)-0.651***(0.242)
0.006
0.002
506

0.149
(0.199)-0.336(0.212)
0.025
0.075
506

0.264
(0.196)-0.102(0.168)
0.068
0.184
506

0.257
(0.179)-0.123(0.183)
0.078
0.186
506

X

X
X

X
X
X

X
X
X
X

Panel B: Born Within 9 Months of Program Ended=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Sample Size

0.251
(0.279)0.177(0.514)
0.887
0.663
214

Panel C: Born More than 9 Months After Program Ended=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Sample Size
Control Structure:
Maternal selection controls + propensity weight
Father selection controls
Cubic in child age in months
Maternal age in years, age interactions-0.011(0.187)-0.351**(0.174)
0.115
0.114
507

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to makethem representative of the target population in the study EAs. The height-for-age z-score is calculated using the 2006 WHO child
growth standards. Specification (1) controls for the gender of the child. Specification (2) adds selection weights and controls
directly for maternal baseline characteristics ( stratum indicators, household asset index, highest grade attended, and an indicator fornever had sex). Specification (3) adds controls for paternal attributes (highest education level, religion, ethnicity, main activity, andlikely HIV status). Specification (4) adds a linear, quadratic, and cubic in child age. Specification (5) adds maternal age andmaternal age interacted with the other baseline covariates. We restrict the sample to respondents who were surveyed during thelatest household survey conducted two years after the program (Round 4). Parameter estimates statistically different than zero at
99% (***), 95% (**), and 90% (*) confidence.

43

Figure I: Research Design
Treatment EAs(88 Clusters)
Conditional(N=61*)

Unconditional(N=27)CCT

CCT

Baseline Dropouts(N=889)Baseline Schoolgirls(N=2,907)

CCT

Withinvillage
control

UCT

Withinvillage
control

Control EAs(N=88)

Pure
control
PureControl*In 15 of the 61 conditional treatment clusters only baseline dropouts were treated.

44

Figure II: Monthly marriage and fertility rates for baseline schoolgirls

.005

.01

.015

.02

.025

Panel A: Monthly Fertility Rates among the Baseline Schoolgirls.

During Program

Utero

0

After Program

2008

2009

2010
Year
Control
UCT

2011

2012

CCT

.005

.01

.015

.02

.025

Panel B: Monthly Marriage Rates among the Baseline Schoolgirls

W/in 9 mos

After Program0

During Program
2008

2009

2010
Year
Control
UCT

2011

2012

CCT

Notes: Figures illustrate the smoothed fraction of core respondents who give birth (Panel A) or get married (PanelB) in each month using retrospective information on the month of birth and marriage, respectively.

45

Figure III: Fan regressions of height-for-age z-scores by month of birth, raw and fully adjusted
treatment effects with 95% confidence intervals
Panel A: Baseline Dropouts, CCT

Panel B: Baseline Schoolgirls, CCT

Panel C: Baseline Schoolgirls, UCT

46

FOR ONLINE PUBLICATION
Supplemental Online Appendix for:
When the Money Runs Out:Do Cash Transfers Have Sustained Effects on Human Capital Accumulation?

Sarah Baird*, Craig McIntosh and Berk Özler
*Corresponding author. E-mail: sbaird@gwu.edu

March 30, 2019
This PDF file includes:
Appendix A: Estimation of Treatment Effects on Children
Tables S1 to S11

47

Appendix A: Estimation of Treatment Effects on Children
This appendix provides an overview of the empirical issues involved in estimating
treatment effects on child outcomes when the intervention under investigation targets prospective
mothers and starts prior to their pregnancies. As the intervention may have altered the compositionof children subsequently observed, we suggest a simple sequence of assumptions and steps in an
attempt to move from the total reduced-form effect of the intervention to a more standard causal
effect on the children actually born.
The natural experimental literature has recognized that maternal selection and differential
mortality represent plausible causal pathways when analyzing child outcomes. Using data fromthe US, Buckles and Hungerman (2013) show that nearly half of the well-documented effects ofseason of birth on later-life outcomes can be explained by variation in the types of women giving
birth across seasons. Aaronson, Lange and Mazumder (2014) show extensive margin selection also
contributes to the quantity-quality tradeoff for children. This phenomenon is well documented in
the developed world, and yet Currie and Vogl (2012) suggest that these extensive margin effects
are likely to be more pronounced in the developing world where differential mortality, as well as
differential fertility, is an operative channel. It has now become standard in the natural experiments
literature to test for the presence of selection effects when studying child outcomes (see, forexample, Almond 2006; Adhvaryu et al. 2016; Black et al. 2017). In many cases in this literature,
the obvious selection effect suggests that the simple casual effects are lower bounds, but we present
a context in which selection and treatment effects go in the same direction. It is therefore criticalto attempt to control for the selection mechanism as a mediator, to isolate how much of theobserved effect may have a simple causal interpretation.
To use counterfactual outcomes to represent impacts on subsequent children, we must
define the universe as being the potential children: all those who might exist under either thetreated or control state.40 Outcome measured for potential child i at time t is Yit . This outcome is
only observed if the child is born and survives, a binary outcome denoted by Sit  1 . The probability
that woman i has a surviving child at time t, as a function of her baseline characteristics, can be
40

This study tracks female respondents and their descendants, so it is concerned with the potential children of a fixed
set of women. We do not attempt to capture all potential children born to the fathers in this study, and to do so would
have needed to specify a group of males at baseline and tracked them. The control for father characteristics in thiscontext therefore sits behind a layer of female selection, and so the assumptions needed to control for father type arestronger than those needed to control for mother type.

48

written as Sit  S ( X i ) , where X i is a set of pre-treatment maternal characteristics. For children whoare born, we observe
Yit  Yit ( xit , ait ; X i , Ait , Zit | Sit  1)

where Ait is the age of the mother at the time at which child data is collected, xit are child-level
determinants of the outcome, ait is child age, and Z it gives attributes of the father.
Critically, in a study tracking potential mothers, X i is observed for all respondents(regardless of whether they had children) and hence can be used to predict fertility within theuniverse of these potential mothers. Controlling for selection into motherhood thus resembles
standard attrition adjustment and requires a (weaker) selection on observables assumption.
Controlling for factors that are observed only among extant children, however, must be done on
the intensive margin, and so resembles mediation analysis as in Baron and Kenny (1986), which
requires substantially stronger assumptions. Specifically, we must now assume that there is a
globally correct functional form across both treatment and control, so that inclusion of themechanism controls does not open a ‘backdoor path’ between the mediator and some other,
unobserved determinant of outcomes (for more discussion of these assumptions, see Sobel 2008;
Flores and Flores-Lagunes 2009; Bullock, Green and Ha 2010; Imai, Tingley and Yamamoto 2013;
Huber 2014; and Heckman and Pinto 2015).
Given these strong assumptions, we now walk through a set of distinct treatment effects
that we may wish to estimate, each of which has a different causal interpretation. We start with thesimple reduced-form impact of the treatment on child outcomes and proceed to add successively
stronger controls until we have isolated the ceteris paribus treatment effect that would have been
observed had an experiment been conducted on the sample of children actually observed, rather
than their mothers. Appendix Figure A1 presents a conceptual framework.

Total effect:(1)

E Yit1  Yit 0 | Sit  1 .

This is the simple difference in outcomes between the children of those exposed to the treatment
versus the control.

49

Correcting for Maternal Type Selection:
We can begin to control for the extensive margin effects of the treatment by modeling theprobability that a child is born to a mother i during epoch t as: Pr(Sit  1)  ( X i , Ti )   it . This
problem is exactly analogous to attrition, and so we can exploit the familiar toolkit to test andcorrect for it (Hanson 1978, Rosenbaum and Rubin 1983). Observational correction can be
conducted using a probit model that regresses a binary indicator for giving birth during an epoch
on a rich set of baseline covariates, a treatment indicator, and the interaction between treatment
and the covariates. We can use this regression to predict the probability of birth for all core
respondents by epoch, and weight the subsequent analysis by the inverse of this probability. Thisis the application of standard attrition-based inverse probability weighting to the fertility problem.
The required assumption is that there be no unobserved determinants of fertility that are correlatedwith the treatment or the treatment*covariate interactions. Regressions weighted by 1

P̂r( Sit  1)

, subject to this assumption, are now representative of the entire original sample of core
respondents and hence not subject to selection effects arising from the decision to give birth ornot. We can also use OLS to control for the same set of maternal baseline characteristics X i toprovide estimates that are “doubly robust” to the extensive margin selection controls (Robins andRotnitzky 2001; Van der Laan and Robins 2003; Bang and Robins 2005). This then provides anestimate of the impact on children if the composition of women who gave birth was identical intreatment and control in each epoch:(2)

E Yit1  Yit 0 | X  X , Pr(S  1| T )  S 

Correcting for Paternal Type Selection:
The next selection margin is father type. In our data structure we do not observe theattributes of the universe of potential fathers, and rather have data on the fathers of children
actually born. We therefore must control for paternal characteristics on the intensive margin rather
than using the selection IPW approach that we use for mothers. The assumptions underlying thesepaternal controls are therefore the strong assumptions of mediation analysis, rather than those of
attrition propensity weighting. Subject to these assumptions, the inclusion of paternal covariates
gives us the expected treatment-control difference holding both maternal and paternal types
constant across the treatment and control groups.

50

(3)

E Yit1  Yit 0 | X  X , Z (T )  Z , Pr(S  1| T )  S 

Correcting for Child Age:
Differences in the composition of child age across treatment and control can lead to large
differences that are, in fact, completely trivial. If, for example, the treatment led to a delay in births,
then the treatment children will be younger on average and hence may perform more poorly on abroad range of tasks than the control children.41 We can recover a meaningful treatment effect bycomparing children in treatment and control at the same age. We achieve this by including linear,quadratic, and cubic controls for child age in months in our regressions:(4)

E Yit1  Yit 0 | a(T )  a , X  X , Z (T )  Z , Pr(S  1| T )  S 

Direct Treatment Effect:
Maternal age represents a potentially important mechanism for improvements in childoutcomes for the same set of mothers, even though it represents an extensive margin effect in thatchanges in maternal age must necessarily lead to a different set of children being born. It is
possible, for example, that an intervention that, all else equal, simply delayed fertility from age 13
to age 18 would lead to improved child outcomes due to increased gynecological maturity. Effects
driven only by changes in age therefore have a meaningful causal interpretation that can be seen
as ceteris paribus for mothers even though it operates on the extensive margin for children. To
control for age as a mediating variable, we can include age and A * X interactions as covariates.
Subject to strong assumptions of (i) selection on observables in the fertility equation, and(ii) correct functional form and common support in the Barron-Kenny controls for the mechanisms,
the resulting adjusted difference provides the ‘direct’ treatment effect of the program on a sample
of children made homogeneous across treatment and control by reweighting and regression
adjustments. The result is a suggestive answer to an obvious policy question: “Does theintervention confer a protective effect on a given child?”(5)

E Yit1  Yit 0 | a(T )  a , Z (T )  Z , X  X , A(T )  A, Pr(S  1| T )  S 

41

Conversely, as shown in Appendix Figure A2, the mean height-for-age z-score in our control group starts out very
close to the mean of the reference group at birth, but declines steadily and rapidly as children get older, ending up
almost two standard deviations below the global distribution by the time they are 36 months old. This seems to be acommon pattern in poor countries (see, for example, Figure 1 in Barham, Macours and Maluccio 2013). Hence,comparing a younger cohort of children in the treatment group to an older cohort in control would spuriously show
lower stunting in the treatment group in the absence of any meaningful effects on height.

51

Figure A1: Conceptual Framework for Causal Pathways to Child Treatment Effects
Treatment

Ti :Mother:Sit ( X , T )  1 Birth Outcome: Is a child born in this interval?

AitC (T ) : Birth Timing: Child Age
AitM (T ) : Birth Timing: Maternal Age

FatherZ i (T ) : Father Selection

Maternal Selection effects that alter theidentity of the woman who gives birthChild Selection effects that alter theidentity of the child who is born

Child
Direct Treatment effect on the child
actually born

D1. Direct impacts

-.5
-1
-1.5
-2

Height for Age

0.5

Figure A2. Height-for-age z-score by age in months (control group)3

6

9 12 15 18 21 24 27 30 33 36 39 42 45 48 51 54 57 60
Age in Months
Males

Females52

References (for Appendix A)
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Extensive and Intensive margins. American Economic Review 104 (11): 3701-3724.
Adhvaryu, Achyuta, Prashant Bharadwaj, James Fenske, Anant Nyshadham, and Richard
Stanley. 2016. Dust and Death: Evidence from the West African Harmattan. CSAE
Working Paper WPS/2016-03. Centre for the Study of African Economies, University of
Oxford.
Almond, D. 2006. Is the 1918 influenza pandemic over? Long-term effects of In Utero Influenza
Exposure in the Post-1940 U.S. Population. Journal of Political Economy 114 (4): 672712.
Baird, Sarah, Craig McIntosh, and Berk Özler. 2011. Cash or Condition? Evidence from a CashTransfer Experiment. Quarterly Journal of Economics 126 (4): 1709-1753.
Baird, Sarah J, Richard S Garfein, Craig T McIntosh, and Berk Özler. 2012. Effect of a cashtransfer programme for schooling on prevalence of HIV and herpes simplex type 2 inMalawi: a cluster randomised trial. The Lancet 379 (9823): 1320-1329.
Baird, Sarah, Jacobus De Hoop, and Berk Özler. 2013. Income shocks and adolescent mental
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Bang, Heejung and James M Robins. 2005. Doubly robust estimation in missing data and causal
inference models. Biometrics 61 (4): 962-973.
Barham, Tania, Karen Macours, and John A Maluccio. 2013. Boys' Cognitive Skill Formation
and Physical Growth: Long-Term Experimental Evidence on Critical Ages for Early
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Baron, Reuben M and David A Kenny. 1986. The moderator--mediator variable distinction insocial psychological research: Conceptual, strategic, and statistical considerations.
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Black, Sandra E, Aline Bütikofer, P Devereux, and K Salvanes. 2017. This Is Only a Test? LongRun and Intergenerational Impacts of Prenatal Exposure to Radioactive Fallout. NBER
Working Paper 18987. National Bureau of Economic Research.
Buckles, Kasey S and Daniel M Hungerman. 2013. Season of birth and later outcomes: Oldquestions, new answers. Review of Economics and Statistics 95 (3): 711-724.
Bullock, John G, Donald P Green, and Shang E Ha. 2010. Yes, but whats the mechanism?(dont
expect an easy answer). Journal of Personality and Social Psychology 98 (4): 550.
Currie, Janet and Tom Vogl. 2012. Early-life health and adult circumstance in developing
countries. NBER Working Paper 18371. National Bureau of Economic Research.
National Bureau of Economic Research.
Flores, Carlos A. and Alfonso Flores-Lagunes. 2009. Identification and Estimation of Causal
Mechanisms and Net Effects of a Treatment under Unconfoundedness. IZA Discussion
Paper No. 4237.
53

Hanson, Robert Harold. 1978. The current population survey: design and methodology
Heckman, James J and Rodrigo Pinto. 2015. Econometric mediation analyses: Identifying thesources of treatment effects from experimentally estimated production technologies withunmeasured and mismeasured inputs. Econometric Reviews 34 (1-2): 6-31.
Huber, Martin. 2014. Identifying causal mechanisms (primarily) based on inverse probability
weighting. Journal of Applied Econometrics 29 (6): 920-943.
Imai, Kosuke, Dustin Tingley, and Teppei Yamamoto. 2013. Experimental designs for
identifying causal mechanisms. Journal of the Royal Statistical Society: Series A(Statistics in Society) 176 (1): 5-51.
Robins, James M and Andrea Rotnitzky. 2001. COMMENTS. Statistica Sinica 920-936.
Rosenbaum, Paul R and Donald B Rubin. 1983. The central role of the propensity score in
observational studies for causal effects. Biometrika 70 (1): 41-55.
Sobel, Michael E. 2008. Identification of causal parameters in randomized studies withmediating variables. Journal of Educational and Behavioral Statistics 33 (2): 230-251.
Van der Laan, Mark J and James M Robins. 2003. Unified methods for censored longitudinal
data and causality. Springer Science & Business Media.

54

Found Indicator
Deceased Indicator
Surveyed Indicator

Table S1: Survey Tracking Rates
Baseline Dropout
Mean (s.d.)Overall
Conditional
Control group
group
(1)
(2)
(3)
0.941
0.923
0.917
(0.236)(0.267)(0.276)
0.007
0.022
0.018
(0.086)(0.147)(0.134)
0.891
0.843
0.837
(0.312)(0.364)(0.370)Baseline Schoolgirl
Mean (s.d.)Control Conditional Unconditional
group
group
Group
(4)
(5)
(6)
0.936
0.955
0.956
(0.245)(0.197)(0.197)
0.005
0.004
0.004
(0.069)(0.066)(0.066)
0.875
0.933
0.930
(0.311)(0.250)(0.256)

Notes: Found indicates that the respondent was located by the enumerator and either surveyed, refused or deceased.

Table S2: Probit Regressions that are the basis for Inverse Propensity Weighting
Outcome variable: Successfully Surveyed in Round 4
Baseline Dropouts

Conditional Treatment
Unconditional Treatment
Baseline Age 14
Baseline Age 15
Baseline Age 16
Baseline Age 17
Baseline Age 18
Baseline Age 19
Baseline Age 20+
Semi-rural stratum
Rural stratum
Highest grade at baseline
Asset index baseline
Never had sex baseline
CCT*Age 14
CCT*Age 15
CCT*Age 16
CCT*Age 17
CCT*Age 18
CCT*Age 19
CCT*Age 20+
CCT*Semi-rural
CCT*Rural
CCT*Highest grade
CCT*Asset index
CTT*Never had sex
UCT*Age 14
UCT*Age 15
UCT*Age 16
UCT*Age 17
UCT*Age 18
UCT*Age 19
UCT*Age 20+
UCT*Semi-rural
UCT*Rural
UCT*Highest grade
UCT*Asset index
UCT*Never had sex
Sample Size

ProbitMarginal
Effects(1)-0.003-0.098-0.162-0.131-0.095-0.077
0.004
0.018
0.022
-0.068-0.018-0.015
0.050
0.127
0.189
0.201
0.122
0.057
0.046
0.040
0.227
0.346
0.013
0.021
-0.056885

Baseline Schoolgirls

Standard Error

p-value

(2)
0.029

(3)
0.920

0.141
0.127
0.119
0.133
0.137
0.139
0.148
0.051
0.059
0.008
0.008
0.046
0.164
0.148
0.143
0.151
0.163
0.167
0.177
0.071
0.095
0.011
0.012
0.063

0.485
0.198
0.267
0.472
0.569
0.977
0.901
0.672
0.255
0.023
0.051
0.293
0.436
0.199
0.153
0.416
0.728
0.782
0.820
0.001
0.000
0.236
0.067
0.372

ProbitMarginal
Effects
(4)
0.048
0.090
0.014
0.017
-0.0150.037
0.019-0.050-0.0000.052
0.024-0.0020.002
0.016-0.016-0.012-0.059-0.096-0.0850.024
0.039-0.085-0.0060.007-0.005-0.006-0.101-0.029-0.047-0.071-0.001-0.005-0.011-0.0570.788-0.0220.018-0.043Standard Error

p-value

(5)
0.015
0.012
0.044
0.037
0.040
0.039
0.042
0.046
0.055
0.017
0.024
0.005
0.005
0.015
0.073
0.070
0.083
0.094
0.104
0.118
0.125
0.049
0.061
0.015
0.008
0.032
0.076
0.053
0.083
0.119
0.119
0.118
0.133
0.049
0.057
0.016
0.008
0.059

(6)
0.007
0.000
0.754
0.653
0.708
0.342
0.647
0.280
0.999
0.001
0.307
0.717
0.723
0.275
0.823
0.859
0.480
0.309
0.420
0.841
0.753
0.085
0.923
0.644
0.568
0.857
0.186
0.585
0.573
0.553
0.996
0.968
0.936
0.253
.
0.168
0.017
0.461

2,273

Notes: Regressions are marginal effects probit models with robust standard errors clustered at the EA level. All regressions are weighted tomake them representative of the target population in the study EAs. The outcome variable is an indicator for being successfully surveyed inRound 4. All interacted baseline covariates are demeaned prior to interaction so that the uninteracted treatment dummies can be interpreted
as effects at the mean of all interacted covariates.

Table S3: Program impacts on educational qualifications and competencies (beneficiaries)
Panel A: Baseline Dropouts
Educational Qualifications=1 if Passed Primary School(PSLC)=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size
Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample Size

=1 if Passed Junior Secondary
School (JCE)=1 if Passed Secondary School(MSCE)

During End of
Program Program

End of
Program(1)
0.030(0.025)
0.328
697

Two Years
Two Years
DuringEnd ofDuring
After
After
Program Program
Program
Program
Program
(2)
(3)
(4)
(5)
(6)
(7)
0.058** 0.081***
0.012
0.049**
0.034
0.004(0.025)(0.026)(0.019) (0.021)(0.022)(0.008)
0.351
0.366
0.085
0.123
0.136
0.008
718
744
697
718
744
697

0.030
(0.039)0.046(0.038)
0.755
0.386
0.496
1,967

0.013
(0.024)0.030(0.026)
0.600
0.488
0.776
2,019

-0.014(0.019)0.017(0.016)
0.166
0.359
0.879
2,047

-0.013(0.022)0.002(0.022)
0.546
0.797
0.144
1,967

0.055*(0.028)0.016(0.045)
0.439
0.148
0.337
2,019

0.033
(0.028)0.010(0.035)
0.565
0.486
0.537
2,047

-0.004*(0.002)-0.006*(0.003)
0.325
0.150
0.004
1,967

Fertilizer
Application

Competencies (Standardized)
Sending aUsing a Calculating
Text
Calculator
Profits
MessageChange
Given

Total
Time
Spent

(8)
0.003
(0.010)
0.025
718

Two Years
After
Program(9)0.016(0.011)
0.026
744

(10)
-0.044(0.069)
0.000
742

(11)
-0.014(0.062)
0.000
741

(12)
0.101
(0.072)
0.000
741

(13)
0.065
(0.071)
0.000
741

(14)
0.094
(0.076)
0.000
742

(15)
-0.007(0.091)
0.000
742

0.005
(0.011)-0.009(0.015)
0.385
0.683
0.054
2,019

0.006
(0.021)-0.065**(0.027)
0.022
0.045
0.170
2,047

0.015
(0.071)
0.096(0.092)
0.378
0.570
0.000
2,048

0.048
(0.071)-0.017(0.057)
0.389
0.685
0.000
2,046

0.077
(0.070)0.161**(0.079)
0.364
0.105
0.000
2,047

0.060
(0.054)0.098(0.064)
0.584
0.249
0.000
2,047

-0.006(0.076)-0.045(0.090)
0.636
0.862
0.000
2,048

-0.113(0.085)-0.118(0.085)
0.963
0.258
0.000
2,048

Two Years After Program

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to make them representative of the target population in the study EAs. Baseline values of the following
variables are included as controls in the regression analyses: age indicators, stratum indicators, household asset index, highest grade attended, and an indicator for never had sex. We restrict the sample to respondents who weresurveyed during the latest household survey conducted two years after the program (Round 4). Competencies represent a set of skills that were anticipated to be sensitive to education and relevant for non-formal employment.
The skills tested included reading and following instructions to apply fertilizer; making correct change during hypothetical market transactions; sending text messages and using the calculator on a mobile phone, and calculating
profits under hypothetical business scenarios. All competency components are standardized to have a mean of zero and a standard deviation of one in the control group. Parameter estimates statistically different than zero at
99% (***), 95% (**), and 90% (*) confidence.

Table S4: Program impacts on sexual behavior (beneficiaries: extensive margin)
Panel A: Baseline Dropouts
Number of Sexual Partners(lifetime)=1 if Ever Had Sex=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size

=1 if Sexually Active During the
Past 12 Months

During
Program

End of
ProgramTwo Years
After
ProgramDuring
Program

End of
ProgramTwo Years
After
ProgramDuring
Program

End of
ProgramTwo Years
After
Program

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

-0.036*(0.020)0.814
698-0.034(0.021)0.918
718-0.004(0.010)
0.976
744

0.004
(0.153)
1.395
698-0.118(0.153)1.734
718-0.023(0.095)2.063
744-0.123*** -0.094**(0.035)(0.037)
0.503
0.674
697
718

-0.046(0.028)0.830
744-0.009(0.017)-0.022(0.021)
0.581
0.551
0.303
1,965

-0.003(0.024)0.003(0.030)
0.864
0.984
0.455
2,016

0.005
(0.035)0.041(0.036)
0.414
0.519
0.701
2,048

-0.023(0.040)-0.044(0.049)
0.699
0.627
0.335
1,964

0.005
(0.048)-0.007(0.036)
0.815
0.969
0.559
2,016

0.005
(0.061)0.108(0.066)
0.142
0.218
1.045
2,047

-0.009(0.023)-0.021(0.030)
0.728
0.768
0.175
1,965

-0.030(0.035)0.037(0.044)
0.177
0.395
0.563
2,048

Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample Size

0.001
(0.029)-0.036(0.032)
0.327
0.514
0.308
2,015

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to make them representative of thetarget population in the study EAs. We correct for inconsistencies in 'ever had sex' across rounds. Baseline values of the following variables are included ascontrols in the regression analyses: age indicators, stratum indicators, household asset index, highest grade attended, and an indicator for never had sex. We
restrict the sample to respondents who were surveyed during the latest household survey conducted two years after the program (Round 4). Parameter
estimates statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

58

Table S5: Program impacts on sexual behavior (beneficiaries: intensive margin)
Panel A: Baseline Dropouts
Age at First Sex=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size
Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample SizeDuring
Program

End of
Program(1)-0.064(0.137)16.250525(2)-0.061(0.144)
16.578625

Two Years
After
Program(3)0.110(0.133)16.790723

0.220(0.146)-0.152(0.179)0.064
0.143
15.731522

0.136(0.130)-0.039(0.189)0.404
0.536
16.393893

0.147(0.146)-0.207(0.127)0.052
0.128
17.1991,494=1 if Older Partner=1 if Use a Condom

During
Program

End ofTwo Years
End of
Program After Program Program

(4)
0.018
(0.054)
0.230
303

(5)
-0.005(0.045)
0.300
427

(6)
0.015
(0.037)
0.309
578

(7)
0.046
(0.037)
0.159
446

Two Years
After
Program(8)
0.030(0.030)0.156
600-0.074(0.050)0.022(0.103)
0.351
0.291
0.193
376

-0.006(0.044)-0.081(0.057)
0.258
0.367
0.274
661

-0.041(0.038)0.018(0.049)
0.248
0.422
0.304
1,162

-0.006(0.055)0.102(0.086)
0.268
0.483
0.247
672

0.015
(0.041)
0.057(0.048)
0.482
0.479
0.268
1,183

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to make them
representative of the target population in the study EAs. Baseline values of the following variables are included as controls in the regression
analyses: age indicators, stratum indicators, household asset index, highest grade attended, and an indicator for never had sex. We restrict the
sample to respondents who were surveyed during the latest household survey conducted two years after the program (Round 4). We correct forinconsistencies in 'ever had sex' across rounds. 'Age at First Sex' is defined for those that had ever had sex. 'Older Partner' is defined as having apartner who is 5 years older or more in the past 12 months. 'Condom Use' is defined as using a condom at last sex with most recent sexual
partner. Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

59

Table S6: Program impacts on health and nutrition (beneficiaries)
Panel A: Baseline Dropouts=1 if Suffers from PsychologicalDistress=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size

Number of Times Respondent
Ate Protein Rich Foods During
the Past 7 Days (out of 21)

During
ProgramTwo Years
End ofDuringEnd of
After
Program
Program Program
Program

Two
Years
After
Program(1)-0.002(0.039)
0.463
698

(2)
0.010
(0.036)
0.314
715

(3)
0.038
(0.042)
0.424
743

(4)
0.326
(0.202)
3.678
698

(6)
0.228
(0.181)3.741
744-0.068**(0.032)-0.139***(0.035)
0.068
0.000
0.372
1,963

-0.037(0.047)-0.026(0.054)
0.860
0.677
0.313
2,013

-0.030(0.032)-0.002(0.046)
0.552
0.627
0.369
2,045

0.385** 0.596*** 0.072(0.195) (0.174) (0.141)
0.445** 0.338** -0.043(0.199) (0.153) (0.240)
0.814
0.215
0.672
0.023
0.001
0.858
3.967
4.052
4.134
1,967
2,018
2,047

(5)
0.224
(0.192)
3.989
718

Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample Size

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions areweighted to make them representative of the target population in the study EAs. Psychological distress is equal to
one if the summed GHQ- 12 score is equal to three or higher, and is zero otherwise. Protein rich foods aredefined as those containing animal proteins, i.e. meat, fish, and eggs. The number of days each item was consumed
over the past week are summed to create the outcome variable. Baseline values of the following variables areincluded as controls in the regression analyses: age indicators, stratum indicators, household asset index, highest
grade attended, and an indicator for never had sex. We restrict the sample to respondents who were surveyed
during the latest household survey conducted two years after the program (Round 4). Parameter estimates
statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

Table S7: Program impacts on labor market outcomes and consumption (beneficiaries: secondary outcomes)
Panel A: Baseline Dropouts
Effective
Labor Income=1 if Any
Daily Wage
(Past 5 Seasons) Wage Work in(Past 7 Days)
2012 USD
Past 3 Months
2012 USD
Two Years After Program=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size

Real Total Household Monthly
Consumption (USD)

During
Program

End of
ProgramTwo Years
After Program-0.228(0.148)
0.753
263

4.129
(8.620)52.840744-0.020(0.037)0.366
744-0.257(1.029)17.502712-1.941*(1.113)20.860719

0.535(1.130)17.977737

0.121(0.424)-0.549*(0.285)
0.278
0.121
0.902
465

7.476
(7.466)10.688(12.721)
0.829
0.420
33.3022,049-0.010(0.030)0.001(0.055)
0.838
0.939
0.250
2,049

3.192**(1.261)-0.586(1.441)0.032
0.030
18.6382,006

3.223**(1.364)-0.880(1.524)0.034
0.044
23.3422,021

2.804*(1.432)-0.817(1.876)0.127
0.137
20.7742,040

Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample Size

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions are weighted to make them
representative of the target population in the study EAs. Effective daily wage is calculated using earnings and activities in the past sevendays. Baseline values of the following variables are included as controls in the regression analyses: age indicators, stratum indicators,
household asset index, highest grade attended, and an indicator for never had sex. We restrict the sample to respondents who were surveyed
during the latest household survey conducted two years after the program (Round 4). Parameter estimates statistically different than zero at
99% (***), 95% (**), and 90% (*) confidence.

61

Table S8: Program impacts on empowerment (beneficiaries: secondary outcomes)
Panel A: Baseline Dropouts
Empowerment
Index ofIndex of SelfIndex of Social
Preferences for
Efficacy
Participation
Child Education(Standardized)(Standardized)(Standardized)=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size

Aspirations(1)-0.041(0.076)
0.000
744

(2)
-0.020(0.079)
0.000
744

(3)
-0.052(0.068)
0.000
744

(4)
-0.221(0.225)
3.267
744

0.059
(0.079)-0.149(0.100)
0.061
0.170
0.000
2,049

-0.004(0.076)-0.106(0.087)
0.343
0.477
0.000
2,049

-0.026(0.068)-0.095(0.069)
0.424
0.393
0.000
2,049

0.235
(0.228)0.004(0.207)
0.379
0.566
3.352
2,049

Panel B: Baseline Schoolgirls=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample Size

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions areweighted to make them representative of the target population in the study EAs. Detail on the construction of
the indices can be found at https://drive.google.com/file/d/1hvI79ltywocFr-pafqz8_Dtg2ZXNhcHd/view.
Aspirations asks the respondent where she sees herself on a 10-step ladder comparing today to five years fromnow, where zero represents the worst possible life she could have and 10 represents the best possible life she
could have. Baseline values of the following variables are included as controls in the regression analyses: age
indicators, stratum indicators, household asset index, highest grade attended, and an indicator for never had sex.
We restrict the sample to respondents who were surveyed during the latest household survey conducted two
years after the program (Round 4). Parameter estimates statistically different than zero at 99% (***), 95%(**), and 90% (*) confidence.

62

Table S9: Program impacts on key outcome using full Round 2 and Round 3 data (baseline dropouts )Panel A: Round 2 Impacts
Highest Grade
Attended=1 if Conditional Schoolgirl
Mean in Control Group
Sample Size
Panel A: Round 3 Impacts=1 if Conditional Schoolgirl=1 if Ever Married=1 if Ever Pregnant

Number of Live
BirthsRound 2
Sample=1 if HIV Positive

Round 2
SampleRound 4
SampleRound 2
SampleRound 4
SampleRound 2 Round 4
Sample Sample

Round 2
SampleRound 4
Sample(1)0.546***(0.068)
6.462
800

(2)
(3)
(4)
(5)
0.579*** -0.102*** -0.140*** -0.053*(0.073)(0.026)(0.029)(0.029)
6.345
0.278
0.291
0.607
697
801
698
801

(6)
-0.057*(0.030)
0.610
698

(8)
-0.003(0.033)
0.521
801

(9)
-0.005(0.033)
0.520
698

(10)
0.032
(0.027)
0.082
417

(11)
0.022
(0.024)0.060
373

Round 3SampleRound 4
SampleRound 4
SampleRound 3 Round 4
Sample Sample

Round 3SampleRound 4
SampleRound 3SampleRound 4
SampleRound 4
SampleRound 3Sample0.522*** 0.558*** -0.139*** -0.157*** -0.079*** -0.081*** -0.097** -0.095**
0.026
0.020
(0.099)(0.102)(0.036)(0.037)(0.026)(0.027)(0.042) (0.044)(0.025)(0.023)
Mean in Control Group
7.078
6.967
0.571
0.575
0.783
0.784
0.817
0.819
0.105
0.094
Sample Size
801
718
801
718
801
718
801
718
763
694
Notes: Regressions are OLS models with robust standard errors clustered at the EA level. We correct for inconsistencies in 'ever married' and 'ever pregnant'across rounds. All regressions are weighted to make them representative of the target population in the study EAs. Baseline values of the following variables
are included as controls in the regression analyses: age indicators, stratum indicators, household asset index, highest grade attended, and an indicator for never
had sex. Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

Table S10: Program impacts on key outcome using full Round 2 and Round 3 data (baseline schoolgirls )Panel A: Round 2 Impacts
Highest Grade
Attended=1 if Conditional Schoolgirl=1 if Unconditional Schoolgirl
p-value UCT vs. CCT
p-value Treatment
Mean in Control Group
Sample Size
Panel A: Round 3 Impacts=1 if Ever Married=1 if Ever Pregnant

Number of Live
Births=1 if HIV Positive

Round 2
SampleRound 4
SampleRound 2
SampleRound 4
SampleRound 2
SampleRound 4
SampleRound 2 Round 4
Sample Sample

Round 2
SampleRound 4
Sample(1)
0.081(0.089)0.134(0.107)
0.644
0.407
8.597
2,146

(2)
0.078
(0.090)0.122(0.109)
0.708
0.469
8.590
1,965

(3)
(4)
0.006
0.000
(0.012)(0.012)-0.030** -0.033***(0.012)(0.012)
0.014
0.026
0.022
0.023
0.047
0.047
2149
1,967

(5)
0.014
(0.014)-0.012(0.017)
0.194
0.404
0.092
2,148

(6)
0.008
(0.015)-0.013(0.017)
0.314
0.600
0.092
1,966

(8)
0.019
(0.014)0.013(0.017)
0.773
0.302
0.056
2,148

(9)
0.023*(0.014)0.013(0.017)
0.641
0.209
0.055
1,966

(10)
-0.020**(0.009)-0.018(0.012)(0.818)(0.080)
0.030
1,287

(11)
-0.020**(0.009)-0.015(0.012)
0.616
0.112
0.026
1,192

Round 3SampleRound 4
SampleRound 3SampleRound 3SampleRound 4
SampleRound 3 Round 4
Sample Sample

Round 3SampleRound 4
SampleRound 4
Sample=1 if Conditional Schoolgirl

0.102
0.126*-0.008-0.010
0.035
0.027
0.006
0.003
-0.004-0.003(0.072)(0.069)(0.023)(0.024)(0.027)(0.027)(0.021) (0.022)(0.011)(0.011)=1 if Unconditional Schoolgirl
0.099
0.103
-0.075*** -0.083*** -0.059** -0.063** -0.050* -0.055*-0.020*-0.019*(0.117)(0.121)(0.023)(0.024)(0.027)(0.028)(0.027) (0.030)(0.012)(0.012)p-value UCT vs. CCT
0.975
0.854
0.024
0.018
0.006
0.009
(0.069)
0.075
0.243
0.237
p-value Treatment
0.323
0.174
0.005
0.004
0.019
0.025
(0.148)
0.151
0.247
0.249
Mean in Control Group
9.699
9.677
0.180
0.180
0.248
0.247
0.201
0.199
0.037
0.035
Sample Size
2,176
2,019
2,175
2,018
2,176
2,019
2,176
2,019
2,136
2,002
Notes: Regressions are OLS models with robust standard errors clustered at the EA level. We correct for inconsistencies in 'ever married' and 'ever pregnant'across rounds. All regressions are weighted to make them representative of the target population in the study EAs. Baseline values of the following variables
are included as controls in the regression analyses: age indicators, stratum indicators, household asset index, highest grade attended, and an indicator for never
had sex. Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

64

Table S11: Attrition Analysis for Primary Round 4 Outcomes (Baseline Dropouts)
Dependent Variable: =1 if Conditional Schoolgirl
Lower Bounds:
Outcomes
Highest Grade CompletedCompetencies Score (Standardized)=1 if Ever Married=1 if Ever Pregnant
Number of Live Births= if HIV Positive=1 if Anemic
Opportunity Cost of Time
Typical Daily Wage in Last Three
Months
Proportion of Hours Spent in SelfEmployment or Paid Work in Past
Super Index of Overall
Empowerment (Standardized)
Change in Subjective Wellbeingfrom Five Years Ago to Today(-) .25 SD(1)0.420***(0.116)-0.025(0.048)-0.138***(0.027)-0.059***(0.018)-0.199***(0.044)-0.021(0.024)-0.002(0.029)-0.146**(0.066)-0.216***(0.055)-0.020***(0.007)-0.175***(0.063)-0.319(0.200)

Unadjusted(-) .1 SD
Lee
(2)
(3)
(4)
0.561*** 0.616*** 0.621***(0.114)(0.125)(0.125)
0.024
0.061
0.064
(0.047)(0.057)(0.057)-0.119*** -0.106*** -0.107***(0.027)(0.032)(0.032)-0.045*** -0.040*-0.040*(0.017)(0.021)(0.021)-0.162*** -0.127** -0.147***(0.044)(0.052)(0.054)-0.0020.019
0.012(0.024)(0.026)(0.026)
0.024
0.045
0.039
(0.028)(0.035)(0.035)-0.084-0.038-0.037(0.065)(0.079)(0.079)-0.173*** -0.141** -0.140**(0.054)(0.068)(0.068)-0.015**-0.011-0.011(0.007)(0.009)(0.009)-0.128**-0.097-0.083(0.062)(0.074)(0.074)-0.157-0.091-0.032(0.198)(0.232)(0.232)IPW

Upper Bounds(5)
0.606***(0.128)0.065(0.057)-0.108***(0.033)-0.041**(0.021)-0.145***(0.055)0.007(0.026)0.041(0.035)-0.041(0.079)-0.132*(0.069)-0.012(0.009)-0.073(0.075)-0.050(0.235)Lee(+) .1 SD (+) .25 SD
(6)
(7)
(8)
0.632*** 0.750*** 0.891***(0.125)(0.113)(0.114)0.089
0.090* 0.139***(0.056)(0.047)(0.047)-0.112*** -0.093*** -0.073***(0.032)(0.027)(0.027)-0.044**-0.026-0.012(0.021)(0.017)(0.017)-0.153*** -0.113** -0.076*(0.053)(0.044)(0.045)0.011
0.023
0.041*(0.026)(0.024)(0.024)0.038
0.059** 0.086***(0.035)(0.028)(0.028)0.065-0.0020.060(0.052)(0.064)(0.064)-0.074-0.115** -0.071(0.055)(0.054)(0.055)-0.007-0.008-0.003(0.008)(0.007)(0.007)-0.065-0.065-0.017(0.072)(0.061)(0.061)
0.048
0.059
0.221
(0.226)(0.196)(0.196)

Notes: Regressions examine extensive margin outcomes using OLS models with robust standard errors clustered at the EA level. Eachcoefficient in this table comes from a different regression of the outcome on a dummy for treatment. Column (4) re-presents the main results
using sampling weights. Column (5) weights by attrition propensity weights, using the standard battery of covariates and their interactions withthe treatment to predict attrition. Columns (3) and (6) provide the lower and upper bounds for the treatment effects using Lee Bounds. Columns(1), (2), (7), and (8) use survey weights and impute missing outcomes by taking the treatment-arm specific mean and adding (subtracting) an
amount equal to .1 or .25 of the standard deviation of the outcome in that arm. Baseline values of the following variables are included ascontrols in the regression analyses: age indicators, stratum indicators, household asset index, highest grade attended, an indicator for never hadsex, and whether the respondent participated in the pilot phase of the development of the testing instruments. Parameter estimates statisticallydifferent than zero at 99% (***), 95% (**), and 90% (*) confidence.

Table S12: Attrition Analysis for Primary Round 4 Outcomes (Baseline Schoolgirls: CCT vs. Control/UCT vs. Control)
Dependent Variable: =1 if Conditional
Dependent Variable: =1 if Unconditional Schoolgirl
Schoolgirl
Unadjusted

Lower Bounds:
Outcomes
Highest Grade CompletedCompetencies Score (Standardized)=1 if Ever Married=1 if Ever Pregnant
Number of Live Births= if HIV Positive=1 if Anemic
Opportunity Cost of Time
Typical Daily Wage in Last Three
Months
Proportion of Hours Spent in SelfEmployment or Paid Work in Past
Super Index of Overall
Empowerment (Standardized)
Change in Subjective Wellbeingfrom Five Years Ago to Today(-) .25 SD (-) .1 SD
(1)
0.049
(0.075)0.031(0.056)-0.068**(0.027)-0.056*(0.034)-0.020(0.036)-0.013(0.018)-0.020(0.027)-0.166*(0.087)-0.048(0.056)-0.001(0.005)-0.007(0.076)0.101(0.168)(2)
0.103(0.075)0.060(0.056)-0.054**(0.027)-0.041(0.033)-0.001(0.036)-0.005(0.018)-0.005(0.027)-0.105(0.086)-0.026(0.055)0.002(0.005)0.023(0.076)0.189(0.169)

Lee
(3)
0.041
(0.084)-0.045(0.050)-0.065**(0.027)-0.046(0.035)-0.027(0.035)-0.057***(0.008)-0.031(0.033)-0.343***(0.060)-0.131***(0.035)-0.010***(0.003)-0.079(0.072)-0.142(0.157)Upper Bounds

IPW
Lee

(4)
0.120
(0.080)0.065(0.058)-0.035(0.027)-0.024(0.034)0.020(0.036)-0.001(0.019)0.012(0.031)-0.051(0.101)-0.011(0.058)0.003(0.005)0.049(0.082)0.276(0.187)(5)
0.122(0.080)0.066(0.058)-0.035(0.028)-0.025(0.034)0.020(0.037)-0.002(0.020)0.011(0.031)-0.049(0.100)-0.009(0.058)0.004(0.005)0.046(0.082)0.275(0.189)(6)
0.208***(0.075)0.129**(0.060)-0.018(0.027)-0.001(0.033)0.044(0.036)0.002(0.020)0.029(0.031)-0.015(0.102)-0.003(0.061)
0.005(0.005)0.121(0.085)0.706***(0.173)

Unadjusted

Lower Bounds:(+) .1 SD (+) .25 SD (-) .25 SD(-) .1 SD

Lee

(7)
(8)
(1)
(2)
(3)
0.174** 0.228***
0.055
0.106
0.052
(0.075)(0.076)(0.112)(0.112)(0.132)0.099* 0.129**
0.077
0.106*
0.028(0.056)(0.056)(0.061)(0.060)(0.067)-0.035-0.020-0.047-0.033-0.049(0.027)(0.027)(0.044)(0.044)(0.045)-0.022-0.007-0.036-0.021-0.034(0.033)(0.033)(0.040)(0.040)(0.042)0.025
0.044-0.067-0.049-0.094*(0.036)(0.036)(0.045)(0.044)(0.049)0.005
0.013-0.022-0.012-0.055***(0.018)(0.018)(0.021)(0.021)(0.008)0.016
0.031 -0.093*** -0.076*** -0.105***(0.027)(0.028)(0.029)(0.029)(0.031)-0.0220.039 -0.208*** -0.152** -0.320***(0.086)(0.087)(0.068)(0.067)(0.062)0.005
0.027-0.0080.016-0.177***(0.054)(0.053)(0.097)(0.097)(0.038)0.005
0.007-0.003-0.000-0.021***(0.005)(0.005)(0.007)(0.007)(0.003)0.063
0.093 -0.199*** -0.168** -0.260***(0.075)(0.075)(0.075)(0.075)(0.071)0.306* 0.394**
0.019
0.104
-0.108(0.172)(0.174)(0.175)(0.174)(0.190)Upper Bounds

IPW
Lee

(4)
(5)
(6)
0.095
0.095
0.210*(0.129) (0.129)(0.123)0.098
0.101 0.176***(0.067) (0.068)(0.063)-0.010-0.0100.010(0.046) (0.048)(0.047)-0.0010.000
0.027(0.042) (0.043)(0.039)-0.024-0.0220.002(0.046) (0.048)(0.046)-0.002-0.0020.001(0.023) (0.023)(0.025)-0.065* -0.067** -0.054(0.033) (0.033)(0.035)-0.115-0.112-0.083(0.074) (0.071)(0.079)
0.036
0.036
0.052
(0.104) (0.105)(0.109)
0.002
0.001
0.004
(0.008) (0.008)(0.008)-0.159* -0.156*-0.079(0.081) (0.082)(0.089)0.176
0.174 0.515***(0.190) (0.190)(0.179)(+) .1 SD (+) .25 SD
(7)
(8)
0.175
0.226**(0.113) (0.115)
0.144** 0.173***(0.059) (0.058)-0.014-0.000(0.043) (0.043)-0.0020.013(0.040) (0.040)-0.024-0.006(0.043) (0.043)
0.000
0.010
(0.021) (0.021)-0.053*-0.036(0.029) (0.029)-0.078-0.022(0.065) (0.064)
0.048
0.072
(0.097) (0.097)
0.003
0.005
(0.007) (0.007)-0.127*-0.097(0.075) (0.075)
0.217
0.301*(0.172) (0.172)

Notes: Regressions examine extensive margin outcomes using OLS with robust standard errors clustered at the EA level. Each coefficient in this table comes from a different regression of the outcome on a dummy for treatment. Column(4) re-presents the main results using sampling weights. Column (5) weights by attrition propensity weights, using the standard battery of covariates and their interactions with the treatment to predict attrition. Columns (3) and (6) provide
the lower and upper bounds for the treatment effects using Lee Bounds. Columns (1), (2), (7), and (8) use survey weights and impute missing outcomes by taking the treatment-arm specific mean and adding (subtracting) an amount equal to.1 or .25 of the standard deviation of the outcome in that arm. Baseline values of the following variables are included as controls in the regression analyses: age indicators, stratum indicators, household asset index, highest grade attended,
an indicator for never had sex, and whether the respondent participated in the pilot phase of the development of the testing instruments. Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*) confidence.

Table S13: Attrition Analysis for Primary Round 4 Outcomes (Baseline Schoolgirls: CCT vs. UCT)
Dependent Variable: =1 if Unconditional Schoolgirl
Unadjusted

Lower Bounds:
Outcomes
Highest Grade CompletedCompetencies Score (Standardized)=1 if Ever Married=1 if Ever Pregnant
Number of Live Births= if HIV Positive=1 if Anemic
Opportunity Cost of Time
Typical Daily Wage in Last Three
Months
Proportion of Hours Spent in SelfEmployment or Paid Work in Past
Super Index of Overall
Empowerment (Standardized)
Change in Subjective Wellbeingfrom Five Years Ago to Today(-) .25 SD(-) .1 SDLee(1)-0.058(0.116)0.009(0.069)-0.013(0.048)-0.013(0.045)-0.083(0.051)-0.015(0.027)-0.093**(0.037)-0.084(0.093)0.050(0.102)-0.006(0.009)-0.241**(0.097)-0.221(0.207)(2)-0.022(0.117)0.029(0.068)-0.003(0.047)-0.003(0.044)-0.069(0.050)-0.007(0.027)-0.078**(0.037)-0.047(0.091)
0.063(0.102)-0.004(0.009)-0.219**(0.098)-0.160(0.206)(3)-0.027(0.129)0.015(0.072)0.013(0.049)0.013(0.046)-0.051(0.054)0.004(0.029)-0.072*(0.041)-0.119(0.095)-0.058(0.046)-0.013*(0.007)-0.243**(0.104)-0.203(0.219)Upper Bounds

IPW
Lee

(4)
-0.021(0.129)0.029(0.072)0.011(0.049)0.010(0.046)-0.053(0.053)0.003(0.029)-0.074*(0.042)-0.040(0.106)0.079(0.108)-0.003(0.009)-0.221**(0.106)-0.134(0.221)(5)-0.020(0.129)0.032(0.073)0.009(0.050)0.010(0.047)-0.052(0.054)0.003(0.029)-0.075*(0.041)-0.035(0.103)0.077(0.108)-0.003(0.010)-0.214**(0.107)-0.134(0.221)(6)-0.005(0.127)0.039(0.070)0.006(0.049)0.006(0.047)-0.061(0.053)-0.006(0.028)-0.086**(0.042)-0.037(0.107)0.080(0.109)-0.003(0.009)-0.206*(0.108)-0.073(0.202)(+) .1 SD (+) .25 SD
(7)
0.026
(0.119)0.057(0.067)0.010(0.046)0.011(0.044)-0.051(0.050)0.004(0.027)-0.058(0.037)0.002(0.089)0.082(0.101)-0.002(0.009)-0.189*(0.099)-0.079(0.205)(8)
0.062(0.120)0.078(0.067)0.021(0.045)0.022(0.044)-0.037(0.049)0.011(0.027)-0.043(0.037)0.040(0.088)0.095(0.101)0.000(0.009)-0.167*(0.101)-0.017(0.205)

Notes: Regressions examine extensive margin outcomes using OLS models with robust standard errors clustered at the EA level. Eachcoefficient in this table comes from a different regression of the outcome on a dummy for treatment. Column (4) re-presents the main results
using sampling weights. Column (5) weights by attrition propensity weights, using the standard battery of covariates and their interactions withthe treatment to predict attrition. Columns (3) and (6) provide the lower and upper bounds for the treatment effects using Lee Bounds. Columns(1), (2), (7), and (8) use survey weights and impute missing outcomes by taking the treatment-arm specific mean and adding (subtracting) an
amount equal to .1 or .25 of the standard deviation of the outcome in that arm. Baseline values of the following variables are included ascontrols in the regression analyses: age indicators, stratum indicators, household asset index, highest grade attended, an indicator for never hadsex, and whether the respondent participated in the pilot phase of the development of the testing instruments. Parameter estimates statisticallydifferent than zero at 99% (***), 95% (**), and 90% (*) confidence.

Table S14: Heterogeneity of Child Height Mediators by Transfer AmountCore Respondent Outcomes
Mentally Ill
R2(1)=1 if Conditional Schoolgirl(minimum transfer amount)
Household transfer amount, CCT
Individual transfer amount, CCT=1 if Unconditional Schoolgirl(minimum transfer amount)
Household transfer amount, UCT
Individual transfer amount, UCT
Number of observations

R3(2)

Meals Eaten
R4
(3)

R2
(4)

R3
(5)

R4
(6)

-0.132** 0.009-0.0730.462 0.975*** 0.527*(0.054) (0.085) (0.069) (0.412) (0.264) (0.294)
0.031*** 0.002-0.001 -0.142* -0.056-0.060(0.009) (0.013) (0.011) (0.084) (0.080) (0.051)-0.009-0.0270.024
0.212*-0.117-0.134(0.018) (0.020) (0.027) (0.114) (0.081) (0.121)-0.118** -0.010-0.0070.392-0.1440.161(0.060) (0.076) (0.069) (0.371) (0.357) (0.387)
0.009
0.018
0.029
-0.0010.030-0.120(0.015) (0.019) (0.020) (0.065) (0.059) (0.083)-0.023 -0.041** -0.039*** 0.013
0.175
0.071
(0.020) (0.019) (0.015) (0.106) (0.112) (0.126)
2,145
2,170
2,045
2,149
2,175
2,047

Notes: Regressions are OLS models with robust standard errors clustered at the EA level. All regressions
are weighted to make them representative of the target population in the study EAs. Psychological distress isequal to one if the summed GHQ- 12 score is equal to three or higher, and is zero otherwise. Protein richfoods are defined as those containing animal proteins, i.e. meat, fish, and eggs. The number of days each item
was consumed over the past week are summed to create the outcome variable. Baseline values of thefollowing variables are included as controls in the regression analyses: age indicators, stratum indicators,
household asset index, highest grade attended, and an indicator for never had sex. We restrict the sample torespondents who were surveyed during the latest household survey conducted two years after the program(Round 4). Parameter estimates statistically different than zero at 99% (***), 95% (**), and 90% (*)
confidence.

68