metadata: authors: 0: author: Akresh, Richard
1: author: de Walque, Damien
2: author: Kazianga, Harounan
count: Burkina Faso
docna: 0: docna: Cash transfers and child schooling :
            evidence from a randomized evaluation of the role of conditionality
docty: Policy Research Working Paper
theme: Education for all
majtheme: Human development
subtopic: Conditional Cash Transfers,Health Care Services Industry,Disability,Educational Sciences,Services & Transfers to Poor,Gender and Development,Economic Assistance,Access of Poor to Social Services
teratopic: Governance,Urban Development,Education
abstracts: cdata!: The authors conduct a randomized
            experiment in rural Burkina Faso to estimate the impact of
            alternative cash transfer delivery mechanisms on education.
            The two-year pilot program randomly distributed cash
            transfers that were either conditional or unconditional.
            Families under the conditional schemes were required to have
            their children ages 7-15 enrolled in school and attending
            classes regularly. There were no such requirements under the
            unconditional programs. The results indicate that
            unconditional and conditional cash transfer programs have a
            similar impact increasing the enrollment of children who are
            traditionally favored by parents for school participation,
            including boys, older children, and higher ability children.
            However, the conditional transfers are significantly more
            effective than the unconditional transfers in improving the
            enrollment of "marginal children" who are
            initially less likely to go to school, such as girls,
            younger children, and lower ability children. Thus,
            conditionality plays a critical role in benefiting children
            who are less likely to receive investments from their parents.
geo_reg_key: 80475,80468,80473,80474
repnme: repnme: Cash transfers and child schooling :
            evidence from a randomized evaluation of the role of conditionality
display_title: Cash transfers and child schooling :
            evidence from a randomized evaluation of the role of conditionality
listing_relative_url: /research/2013/01/17201151/cash-transfers-child-schooling-evidence-randomized-evaluation-role-conditionality
topicv3: Education m1327048 470,Cash Transfers m1327437 1608,Gender m1327621 615,Health m1504661 3480,Conditional Cash Transfers m1586414 3552
publishtoextweb_dt: 2013-01-01T00:00:00Z
historic_topic: Governance,Urban Development,Education
no_of_pages: 57
model_extractions: WPS6340 Policy Research Working Paper 6340 Impact Evaluation Series No. 82

# Cash Transfers and Child Schooling

Evidence from a Randomized Evaluation of the Role of Conditionality _Richard Akresh Damien de Walque Harounan Kazianga_ The World Bank Development Research Group Human Development and Public Services Team January 2013
Policy Research Working Paper 6340

# **Abstract**

The authors conduct a randomized experiment in rural Burkina Faso to estimate the impact of alternative cash transfer delivery mechanisms on education. The twoyear pilot program randomly distributed cash transfers that were either conditional or unconditional. Families under the conditional schemes were required to have their children ages 7–15 enrolled in school and attending classes regularly. There were no such requirements under the unconditional programs. The results indicate that unconditional and conditional cash transfer programs have a similar impact increasing the enrollment of children who are traditionally favored by parents for school participation, including boys, older children, and higher ability children. However, the conditional transfers are significantly more effective than the unconditional transfers in improving the enrollment of “marginal children” who are initially less likely to go to school, such as girls, younger children, and lower ability children. Thus, conditionality plays a critical role in benefiting children who are less likely to receive investments from their parents.

This paper is a product of the Human Development and Public Services Team, Development Research Group. It is part of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy discussions around the world. Policy Research Working Papers are also posted on the Web at http://econ.worldbank.org. The authors may be contacted at akresh@illinois.edu, ddewalque@worldbank.org and harounan.kazianga@okstate.edu.

_The Impact Evaluation Series has been established in recognition of the importance of impact evaluation studies for World Bank operations and for development in general. The series serves as a vehicle for the dissemination of findings of those studies. Papers in this series are part of the Bank’s Policy Research Working Paper Series. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent._ Produced by the Research Support Team
# **Cash Transfers and Child Schooling: Evidence from a Randomized Evaluation of the Role of Conditionality**<sup>∗</sup>

Richard Akresh University of Illinois at Urbana-Champaign Damien de Walque The World Bank Harounan Kazianga Oklahoma State University _Keywords_ : Cash transfers; Conditionality; Education; Africa _JEL classification_ : I21; I25; I38; J13; O15; C93

* These data were collected for a project evaluating social protection strategies in Burkina Faso, which greatly benefited from the support of Marie-Claire Damiba, Seydou Kabré and Victorine Yameogo from the Secrétariat Permanent du Comité National de Lutte contre le SIDA et les Infections Sexuellement Transmissibles in Burkina Faso and Nono Ayivi-Guedehoussou, Hans Binswanger, Ousmane Haidara, Timothy Johnston, Mead Over, and Tshiya Subayi-Cuppen at the World Bank. Data collection was supervised by Robert Ouedraogo, Jean-Pierre Sawadogo, Bambio Yiriyibin and Pam Zahonogo from the University of Ouagadougou. The project is funded by the NBER Africa Project and the following World Bank trust funds grants: Strategic Impact Evaluation Fund (SIEF), Bank-Netherlands Partnership Program (BNPP), Gender Action Plan (GAP), Knowledge for Change Program (KCP), WB-DFID Evaluation of the Community Response to HIV and AIDS, Trust Fund for Environmentally & Socially Sustainable Development (TFESSD), and Luxembourg Poverty Reduction Partnership (LPRP). The authors thank Emilie Bagby, German Caruso, Christine Jachetta, Marleen Marra, and Nga Thi Viet Nguyen for excellent research assistance. The authors also thank Adam Wagstaff and seminar participants at Dalhousie, Oklahoma State, and the World Bank for helpful comments on earlier drafts. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the World Bank, its Executive Directors, or the countries they represent.

Contact Information: Richard Akresh, University of Illinois at Urbana-Champaign, Department of Economics, 1407 West Gregory Drive, David Kinley Hall, Room 101, Urbana, IL 61801.Email: akresh@illinois.edu; Damien de Walque, The World Bank, Development Research Group, 1818 H Street, N.W., Washington, D.C., 20433. Email: ddewalque@worldbank.org; Harounan Kazianga, Oklahoma State University, Department of Economics, 324 Business Building, Stillwater, OK 74708. Email: harounan.kazianga@okstate.edu
# **1. Introduction**

Conditional cash transfer (CCT) programs are one of the most popular social sector interventions in developing countries.<sup>1</sup> While program design details vary, they all transfer resources to poor households conditional on the household taking active measures to increase the human capital of their children (enrolling their children in school, maintaining their attendance, and taking them for regular health care visits). In making transfers conditional, interventions seek to encourage human capital accumulation and break a cycle where poverty is transmitted across generations. While both CCT and unconditional cash transfer (UCT) programs provide poor households with resources, UCT programs do not impose conditionality constraints. An important question is whether and how conditions imposed by CCTs influence the outcomes they seek to improve.

In this paper, we present evidence of the education impacts from a unique cash transfer pilot program in rural Burkina Faso, the Nahouri Cash Transfers Pilot Project (NCTPP). The NCTPP incorporated a random experimental design to evaluate the relative effectiveness of the following four cash transfer programs targeting poor households in the same setting in rural Burkina Faso: conditional cash transfers given to fathers, conditional cash transfers given to mothers, unconditional cash transfers given to fathers, and unconditional cash transfers given to mothers. This paper focuses on the differential impact of conditional and unconditional cash transfers on the educational outcomes of children between the ages of 7 to 15.

The main contribution of our paper is to develop and empirically test the hypothesis that CCTs are more effective than UCTs in improving the enrollment of “marginal children”, those who are initially not enrolled in school or are less likely to go to school, such as girls, younger

> 1 As of 2011, eighteen countries in Latin America and the Caribbean had implemented CCT programs, with four others in the process of designing ones (Stampini and Tornarolli, 2012). These CCT programs have approximately 135 million beneficiaries, about a quarter of the population. In terms of program size, the budget costs range from 0.50 percent of GDP in Brazil and Mexico to 0.08 percent in Paraguay and Chile (Fiszbein and Schady, 2009). In addition to Latin America, a growing number of countries in Asia have implemented CCT programs, while in Africa, several CCT pilot programs have begun in Kenya, South Africa, Malawi, and Morocco.

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children, and lower ability children. We start from the observation that parents in this setting often decide strategically to invest more in the education of some of their children (Akresh, Bagby, de Walque, and Kazianga, 2012a, 2012b highlight in our baseline survey strategic enrollment choices by parents based on child ability). Because our sample population includes all children (boys and girls ages 7-15), we can explicitly measure the differential impacts of conditionality on “marginal” children compared to other children.

There is credible evidence that both types of transfer schemes can substantially improve child education.<sup>2</sup> However, only one published study explicitly compares conditional and unconditional cash transfers in the same context (Baird, McIntosh, and Özler, 2011).<sup>3</sup> They examine in Malawi the impact of conditionality on the drop-out rates of adolescent girls enrolled at baseline and find that CCTs are more effective than UCTs for these girls. As we discuss in greater detail below, our results are different from theirs. We find that CCTs are more effective than UCTs for marginal children (a group that might include adolescent girls in Malawi), while UCTs are equally effective as CCTs for non-marginal children. Since our cash transfer intervention focused on a broader range of child age and gender and on both margins of school enrollment (bringing non-enrolled children into school and reducing drop-outs), we are able to explain how conditionality works and specifically for which types of children it works best.

> 2 For the evidence of CCT impacts on education in Mexico see Schultz (2004), Behrman, Sengupta, and Todd (2005), de Janvry et al. (2006), and Attanasio, Meghir, and Santiago (2011); in Colombia see Attanasio et al. (2010) and Barrera-Osorio et al. (2012); in Nicaragua see Maluccio and Flores (2005) and Macours, Schady, and Vakis (2012); in Honduras see Glewwe and Olinto (2004); in Brazil see Bursztyn and Coffman (2012) and Glewwe and Kassouf (2012); in Cambodia see Filmer and Schady (2011). For the evidence of UCT education impacts in Ecuador see Paxson and Schady (2010) and Edmonds and Schady (2012); in South Africa see Case, Hosegood, and Lund (2005) and Edmonds (2006).

> 3 Other studies use accidental glitches in program implementation to compare UCTs and CCTs. Some households in Mexico (de Brauw and Hoddinott, 2011) and Ecuador (Schady and Araujo, 2008) did not think the cash transfer program was conditional, and school enrollment was lower among those households who thought the transfers were unconditional. Evaluations using structural models conduct counterfactual analyses that find UCTs would have no impact or a much lower impact on enrollment (Bourguignon, Ferreira and Leite, 2003; Todd and Wolpin, 2006).

3
We are aware of one other cash transfer project in Morocco, with a design similar to ours, which examines the impact of conditionality on educational outcomes. The Burkina Faso and Morocco projects were conducted independently but at exactly the same time. Preliminary results of the Morocco experiment indicate no differences between conditional and unconditional cash transfers (Benhassine, Devoto, Duflo, Dupas, Pouliquen, 2012). The authors offer several potential explanations for their results. In the Morocco experiment, child enrollment and attendance were high, so the conditionality constraints were inframarginal, while in Burkina Faso, many children were not enrolled at the baseline, so conditionality was binding. In addition, because program registration in Morocco for all treatments was done at the schools, including those receiving unconditional transfers, this could have increased parents’ views about returns to education and the quality of schooling or confused them about the role of conditionality. In Burkina Faso, transfers were delivered in each treatment village in a central location away from the schools by a village committee set up by the government to administer the cash transfer pilot. As a consequence, in the UCT villages, there was no explicit or implicit linking of the cash transfers to schooling, which enables us to capture the pure income effect of the UCTs.

Our results indicate that CCTs are more effective than UCTs in improving the enrollment of “marginal” children, those who are initially not enrolled in school or are less likely to go to school, including girls, younger children, and lower ability children. With yearly transfer amounts of $17.6 for children ages 7-10 and $35.2 for children ages 11-15, we find that CCTs led to statistically significant increases in enrollment of 20.3 percent for girls, 37.3 percent for younger children, and 36.2 percent for low ability children relative to mean enrollment in those sub-groups. For these same categories of marginal children, UCTs either had no statistically 4
significant impact or showed an impact that was significantly smaller than the CCT effect.<sup>4</sup> However, we find that UCTs and CCTs have similar impacts in increasing the enrollment of children who are already enrolled at baseline or are traditionally prioritized by parents for school participation, including boys, older children, and higher ability children. We find enrollment increases due to CCTs and UCTs respectively of 21.8 and 22.2 percent for boys, 17.4 and 14 percent for older children, and 27.0 and 28.5 percent for higher ability children.

These results shed new light on the role of conditionality in cash transfer programs. In resource-poor settings, both UCTs and CCTs relax the budget constraint and allow households to enroll more of the children they would traditionally prioritize for human capital investments. But the conditions attached to CCTs play a critical role in improving the outcomes of children for whom parents are less likely to invest.

The remainder of the paper is organized as follows. In Section 2, we develop a conceptual framework formulating our hypothesis that CCTs are more effective in improving the schooling outcomes of marginal children. Section 3 describes the context of our experiment and the design of the cash transfer pilot program. Section 4 describes our empirical identification strategy, and Section 5 presents the main results and robustness checks. Section 6 concludes.

# **2. Conceptual Framework: “Marginal Child” Hypothesis**

In this section, we motivate our underlying hypotheses for empirically testing the relative merits of CCTs and UCTs. The conditions attached to CCTs are meant to induce households to behave differently than they would have under UCTs that paid the same amount of cash. By distorting household choices (if conditionality is binding) to achieve a more socially desirable outcome (in this case increased education for marginal children), CCTs can lead to lower household welfare

> 4 With regards to the Malawi evaluation (Baird, McIntosh, Özler, 2011), to the extent that adolescent girls in secondary school (the focus of their study) can be considered as “marginal” children from an education point of view, our marginal child hypothesis would have predicted that CCTs would have been more effective than UCTs.

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compared to UCTs.<sup>5</sup> Another argument against making transfers conditional is that because the conditions need to be verified, CCTs are more expensive per child to implement and administrative capacity to conduct them may not be sufficient in less-developed countries.

Conditionality is often justified by the observed low investment in human capital. This low investment may be due to parents not internalizing positive social externalities of education (de Janvry and Sadoulet, 2005), to parental agency problems whereby parents make education and child labor decisions but do not adequately consider the child’s future welfare (Edmonds, 2008), to parental irrationality, impatience, or lack of self-control (Das, Do, and Özler, 2005), to borrowing constraints or the absence of negative bequests across generations (Martinelli and Parker, 2003), or to underestimates of returns to education (Jensen, 2010). A further justification for conditionality invokes political economy arguments claiming that non-poor individuals would only agree to transfer programs if conditions were in place (Gelbach and Pritchett, 2002).

The common approach in the literature when comparing CCTs and UCTs is to depict investment in human capital against another good (Das, Do and Özler, 2005).<sup>6</sup> This essentially assumes educational investments are homogenous across children, and households differ only in how much they invest in their children. We take a slightly different approach and introduce the idea of a marginal child to motivate our hypotheses. We define a marginal child as one who has a lower tendency to enroll in school absent an external intervention. In contrast, a non-marginal child is one the household would be more likely to enroll even without an external intervention. In the empirical section, we confirm that specific types of children, such as girls or low cognitive ability children, are less likely to be enrolled in the baseline prior to the transfer program.

> 5 This is similar to the textbook example of in-kind versus cash transfers (Cunha, 2010).

> 6 In this section, we use education in our discussion because that is the focus of the empirical analysis. However, our framework can accommodate other types of human capital as well.

6
We illustrate our conceptual framework in Figure 1. Households choose between education and other goods.<sup>7</sup> The minimum desired level of education (for example enrollment and 90 percent attendance) and the threshold for conditionality to be satisfied is represented by point _E_ . In the absence of transfers, the household budget constraint is represented by line _AB_ . Parents make different choices for marginal and non-marginal children<sup>8</sup> : under budget constraint _AB_ , parents invest more in the education of their non-marginal children (point _a_ ) than their marginal children (point _a'_ ). The income elasticity of education is smaller for marginal children than for non-marginal ones so that as income increases the income-consumption curve is represented by the line _OH_ going through points _a_ and _b_ for high ability (non-marginal) children and by the line _OL_ going through points _a'_ and _b'_ for low ability (marginal) children.<sup>9</sup> With UCTs, a household receives a quarterly cash transfer for each child in the relevant age range. This is equivalent to a shift of the budget constraint to the right, bringing the household to the UCT budget constraint _CD_ . Under UCTs, parents increase education more for their non-marginal children (to point _b_ ) compared to the increase for their marginal children (to point _b'_ ). With CCTs, a quarterly cash transfer is paid to households for each child who is enrolled and attends school at least 90 percent of the time (i.e. consumes at least _E_ of education). The budget constraint under CCTs is represented in bold ( _AFc'D_ ) and is kinked at point _E_ . To the right of _E_ , the household receives the CCT, the budget constraint is represented by the line _c'D_ , and it coincides with the UCT budget constraint. To the left of _E_ , the condition is not satisfied,

> 7 Education of marginal and non-marginal children are two distinct goods and households allocate budgets between these two goods and other goods. This distinction between marginal and non-marginal child education could be due to higher effective expenses to educate marginal children (e.g. more grade repetition of marginal children). 8 This feature allows us to accommodate situations where most households do not enroll all of their children, which is common in rural Burkina Faso (Akresh, Bagby, de Walque, and Kazianga, 2012a, 2012b). Baseline data indicate only 24 percent of households enroll all children, and non-marginal children such as boys, high ability children, and older children are more likely to be enrolled.

> 9 While marginal and non-marginal children have different income elasticities, for simplicity, we assume the income elasticity is constant across the income range for each child type.

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the household does not receive the CCT, and the budget constraint reverts to the line _AF_ , along the initial budget constraint. For non-marginal children, the household’s utility is maximized at point _b_ under both the UCT and CCT programs, indicating that both interventions have the same effects on education. However, for marginal children, point _b'_ is unattainable under a CCT. The household chooses point _c'_ , satisfies the education condition _E_ , and receives the transfer. Point _c'_ is preferred to point _a'_ , where the education condition is not satisfied, but the indifference curve at point _b'_ under the UCT would have been preferred to the outcome under the CCT.

Figure 1’s simple framework can motivate a clear empirically testable proposition: when considering only human capital investments, relative to UCTs, CCTs increase investment in human capital of marginal children and no non-marginal child is made worse off. The empirical implications are the following. First, CCTs increase education for marginal children more than UCTs. Second, UCTs and CCTs have similar educational impacts for non-marginal children.

# **3. Context and Experimental Design**

# _3.1 Context_

Burkina Faso offers an important setting for exploring the effects of cash transfers on rural children’s education. Even by African standards, education outcomes in Burkina Faso are poor. In 2010, the net attendance ratio for primary school in rural Burkina Faso was 44.4 (45.5 for boys and 43.1 for girls) and the gross attendance ratio was 64.9 (66.2 for boys and 63.5 for girls) (Institut National de la Statistique et de la Démographie and ICF International, 2012).<sup>10</sup> The cash transfer program was run in Nahouri province in southern Burkina Faso, 100 miles from the capital, Ouagadougou. Households in the region are mainly subsistence farmers

> 10 The primary school net attendance ratio is the percentage of children attending primary school who are of the official school age. The primary school gross attendance ratio is the number of primary school students, irrespective of age, as a percentage of the official primary-school-age population. If there are a significant number of underage or overage students in primary school, the gross attendance ratio is higher than the net attendance ratio.

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growing sorghum and groundnuts. Table 1a shows that for the entire sample (N = 2629 households), there are, on average, 6.6 members in each household, of whom 1.6 are children under 84 months and 1.9 are children of school going age (7 to 15). Mean annual household per capita expenditures (including own consumption) were 99,951 FCFA (approximately $220 USD using the January 2010 exchange rate of $1 USD = 455 FCFA). Of the children ages 7 to 15, 65.7 percent are reported by their parents to be enrolled in school, but when enrollment is measured using school administrative rosters, the enrollment rate is only 49.2 percent, suggesting survey respondents may overstate school participation as Baird and Özler (2012) document.<sup>11</sup> School attendance conditional on enrollment as measured from school rosters is high at 98.1 percent, suggesting that, once enrolled, children are very likely to attend classes. The attendance rates are consistent with other research in Africa using administrative school data (Miguel and Kremer, 2004 in Kenya; Benhassine et al., 2012 in Morocco; Kazianga, de Walque, and Alderman, 2012 in another region of Burkina Faso). Furthermore, at least for Burkina Faso where enrollment is low, they are suggestive of an environment where parents strategically choose which children they register and then make sure the children attend regularly. We also report attendance unconditional on enrollment, a broader measure of school participation that incorporates enrollment and attendance effects. On an average school day, 46.2 percent of children ages 7 to 15 are in class. Mean education expenses per child are $9.66 per year.

> 11 To obtain the school roster information about enrollment and attendance, survey enumerators took the list of children reported to be enrolled by their parents and searched for them in the school’s administrative rosters. After matching the child’s name, they then recorded the child’s enrollment status and the number of days the child was absent or present for each month during the academic year. Unfortunately, we were not able to collect school administrative data for every year for all children. There were 225 school rosters to be collected (3 rounds of data collection for 75 villages), but we could not collect 5 of them due to the school being closed and the teachers and principal having left for summer vacation. In addition, for some children, it was difficult to identify a match between the names on the school and household rosters because many children in a given class often have the same first and last name. For these difficult cases, we used child age, gender, and the mother and father’s names to confirm a match. In Section 5.5, we discuss the robustness checks we perform to confirm there was no differential selection across treatment groups in which children we were not able to collect administrative data for.

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Table 1b focuses on baseline summary statistics for school enrollment and attendance. Columns 1 to 6 disaggregate those statistics by gender, age group, and ability level as measured by the Raven’s raw score.<sup>12</sup> For enrollment using both self-reported and school-based measures and for attendance, we observe that, at baseline, girls are less likely to be enrolled and attend school than boys. A similar pattern of lower enrollment and attendance is observed for younger children<sup>13</sup> (ages 7 to 8) compared to older children (ages 9 to 13) and for children with lower cognitive ability (a Raven’s score below the sample mean) compared to higher ability children (those with a Raven’s score above the mean). All of those baseline differences are statistically significant. These observations at baseline confirm our description of girls, younger children, and lower ability children as categories of “marginal” children in our conceptual framework.

_3.2 Experimental Design: Burkina Faso Nahouri Cash Transfers Pilot Project_ The 75 villages in Nahouri province that each have a primary school were randomly allocated to the following five groups as illustrated in Panel A of Figure 2: (i) conditional cash transfers given to the father, (ii) conditional cash transfers given to the mother, (iii) unconditional cash transfers given to the father, (iv) unconditional cash transfers given to the mother, and (v) a control group.<sup>14</sup> There were 15 villages in each treatment arm and in the control group, and only poor households were eligible to receive a cash transfer.<sup>15</sup> After villages were randomly assigned

> 12 We use the Raven’s Colored Progressive Matrices (CPM) to measure a child’s cognitive ability. The Raven’s CPM is a measure of fluid intelligence or problem solving ability, and it does not require formal schooling to be able to answer the questions (Raven, Raven, and Court, 1998). The test does not depend heavily on verbal skills, making it relatively “culture free” (Borghans, Duckworth, Heckman, and ter Weel, 2008). In the Raven’s test, the child respondent is asked to select the image that is missing in order to complete a picture.

> 13 Age seven is the official school starting age in Burkina Faso, but many children start school at a later age. 14 Due to the low primary school enrollment rates in Burkina Faso, the program intervention focused exclusively on primary schooling as opposed to also covering secondary schools.

> 15 Immediately prior to the baseline survey, we conducted a household census in every village to collect information from each household about living structure (flooring, access to latrine), ownership of assets (plow, cart, draft animals, motorcycle, radio), whether the household head ever attended school, whether the household grows cotton, and whether there is a weekly village market. We combined this information with a Burkina Faso nationally representative household survey (INSD Burkinabe Survey on Household Living Conditions – 2003) to calculate a

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to the five groups defined above, poor households in the treatment villages were randomly assigned to receive that particular type of cash transfer.<sup>16</sup> In our three survey rounds (baseline, one-year follow-up, two-year follow-up) conducted in June 2008, June 2009, and June 2010, we interviewed all poor households in each of the treatment villages who were randomly selected to receive the transfer.<sup>17</sup> In each of these four groups of 15 villages, we interviewed approximately 540 poor households randomly selected to receive transfers. The control group consisted of 615 randomly selected poor households that did not receive cash transfers in the 15 control villages where no households received transfers.<sup>18</sup> In households randomly assigned to CCTs, the mother or father received a quarterly stipend for each child if that child satisfied the following conditions. For children under age seven, receiving the transfer required quarterly visits to the local health clinic for growth monitoring (Akresh, de Walque, Kazianga, 2013). For children ages 7 to 15, receiving the transfer required school enrollment and attendance above 90 percent each quarter.<sup>19</sup> Each child in the CCT households was given a program booklet in which school attendance or health clinic visits were recorded by the school teachers or clinic staff, respectively. The booklets were used to confirm a child’s satisfaction of the conditionality requirements needed to receive CCTs. In addition, 20 percent of these children were randomly selected and a village committee that had been specifically trained to do audits verified the information in the booklets against health clinic

> predicted poverty level for each household and compare that with the national poverty line to determine if a household should be considered poor and eligible to receive cash transfers.

> 16 To minimize child fostering in response to the program introduction and reduce any associated risk of statistical contamination (see Akresh, 2009, for evidence on the relationship between income shocks and child fostering), eligibility for transfers was based only on the children present in the household at the time of the baseline survey. 17 Our research protocol received IRB clearance from the Institutional Review Board at the University of Illinois at Urbana-Champaign (case #08334) and from the Burkina Faso National IRB (“Comité d’Ethique”). 18 Note that the difference between the number of households interviewed and the number used in this paper’s analysis is due to some households being excluded because they had no children ages 7 to 15.

> 19 In the CCT villages, the first payment of the school year was conditional only on school enrollment and not attendance, since attendance cannot be measured in the holiday period preceding the start of the school year.

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and school administrative registers. Based on our discussions with these committees, it appears that conditionality was enforced. Cash transfer take-up rates (the fraction of eligible households receiving transfers for at least some children) in the CCT villages declined as the school year progressed, which is also consistent with conditionality being enforced.<sup>20</sup> In households randomly assigned to UCTs, the mother or father received a quarterly stipend for each child. There were no requirements or conditions linked to receiving the stipend.

CCT and UCT households were told they could use the funds at their convenience and no instructions were given as to how to spend the money. CCT and UCT cash distribution was done separately in each village to minimize any risks of cross-village information contamination of the randomization, since we did not want households in UCT villages to believe that health clinic or school attendance was going to be checked in their villages as well. In addition, each village had only one primary school, and no children attended a primary school that is not in their village.

Furthermore, our program design explicitly assumed each treatment group would receive equal amounts of resources per capita over the two-year pilot, if households randomly allocated to the CCTs fully satisfied conditionality. In practice, because there was not full compliance with conditionality, households receiving UCTs, on average, received more money per capita.

In the CCT and UCT programs, for each child under age seven, the mother or father would receive 4,000 FCFA per year distributed in quarterly payments (approximately $8.8 USD or 4.0 percent of household per capita expenditures). For each child ages 7 to 10 (or in grades 1 to 4 in the CCT villages), the mother or father would receive 8,000 FCFA per year in quarterly payments (approximately $17.6 USD or 8.0 percent of household per capita expenditures), while

> 20 The CCT take-up rates by quarter for school year 2008-2009 are 99.0, 91.0, 90.7, and 85.3 percent, respectively. In school year 2009-2010, the rates are 94.7, 91.6, 89.9, and 89.7 for each quarter, respectively. The take-up rates in the UCT villages are considerably higher. In school year 2008-2009, they are 99.4, 98.8, 98.6, and 94.5 percent for each quarter, respectively. In 2009-2010, they are 99.1, 98.8, 98.5, and 97.1 percent for each quarter, respectively.

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for each child ages 11 to 15 (or in grades 5 or higher but younger than 15 in the CCT villages), the mother or father would receive 16,000 FCFA per year in quarterly payments (approximately $35.2 USD or 16.0 percent of household per capita expenditures). To compare the generosity of this pilot project to other cash transfer programs, we measure the annual transfer amount that each household was eligible for as a fraction of household per capita expenditures and find that at 10.4 percent, the Burkina Faso cash transfer pilot was small in size (see Fiszbein and Schady, 2009 who note CCT program generosity levels of 1, 6, 17, 22, and 29 percent of household expenditures in Bangladesh, Brazil, Colombia, Mexico, and Nicaragua, respectively).

# **4. Empirical Identification Strategy**

The key question we address is whether cash transfers improve educational outcomes, such as enrollment, attendance, and achievement tests, of children ages 7 to 15 in recipient households. To obtain clearer comparisons between the different transfer modalities and to increase statistical power, in the empirical estimations, we pool treatment arms and consider households that were either randomly selected to receive conditional cash transfers or randomly selected to receive unconditional cash transfers (Panel B of Figure 2). This approach combines into one group conditional cash transfers given to fathers or to mothers and into a second group unconditional cash transfers given to fathers or to mothers. With this approach, we highlight the role of conditionality, and we ignore the intra-household allocation aspects of the experimental design.<sup>21</sup> The randomized experimental design provides a strong identification strategy that allows us to attribute differences in outcomes between the treatment and control groups to the impact of the program. We first present results based on a specification that does not include the baseline data and exclusively relies on the random allocation of interventions across villages and on the

> 21 In on-going research analysis, we explore the differential impacts of giving transfers to fathers or mothers.

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data from the final follow-up survey in 2010 (Round 3). We focus on the program effect on the treated households (ATE) and estimate the following regression:

# (1)

where _yihv_ is an educational outcome for child _i_ in household _h_ and village _v_ in Round 3 _, CCThv_ is the treatment indicator that takes the value one if a child lives in a household that was randomly selected to receive conditional cash transfers and zero otherwise, _UCThv_ is the treatment indicator that takes the value one if a child lives in a household that was randomly selected to receive unconditional cash transfers and zero otherwise, _Xihv_ is a vector of child characteristics (gender and age) included to reduce residual variation across arms after randomization, and ε _ihv_ is a random, idiosyncratic error term.

Since our data collection included baseline and follow-up surveys, we can control for differences across villages in the baseline values of the variables. To do so, we use the following difference-in-differences model: (2) where _yihvt_ is an educational outcome for child _i_ in household _h_ in village _v_ and year _t, T2_ and _T3_ are round indicators for the first and second follow-up surveys (Rounds 2 and 3, respectively), _Dj_ is the treatment indicator that takes the value one if a child lives in a household that was randomly selected to receive treatment _j_ (CCT or UCT) and zero otherwise, _Xihvt_ is a vector of child characteristics (gender and age), _Lν_ is a village fixed effect, and ε _ihvt_ is a random, idiosyncratic error term.<sup>22</sup> The impact of transfer scheme _j_ ( _j_ =1, 2) in period _t_ (t=2, 3) is given by _α t j_ , the coefficient of the interaction between the treatment status and the round dummy. Since

> 22 Correlation among the error terms of children living in a village and experiencing similar shocks in the baseline or follow-up rounds, combined with the design effect of our village-level before and after treatment, might bias the OLS standard errors downward, so in all regressions we cluster the standard errors at the village*follow-up level.

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we randomized at the village level and we control for village fixed effects, the treatment dummies ( _Dj_ ’s) would be redundant in Equation 2 and therefore are not included.

Due to logistical reasons, the cash transfer program was unexpectedly launched late by Burkina Faso’s government in the 2008-2009 school year. The first cash payment was only made at the end of November/early December 2008, while the school year started October 1, 2008.

This meant most households were not able to enroll their children during the program’s first year as they did not receive the transfer in time to pay school fees due at the start of the academic year. Subsequently, as we will see when we discuss the results, we do not observe any education impacts during the first year of the program. For this reason, we also present a difference-indifferences specification that only includes the baseline Round 1 data and the follow-up Round 3 data from the 2009-2010 school year. In Equation 3, the round indicator is for the second followup survey (Round 3) conducted in June 2010, and the other variables are as defined previously.

(3)

# **5. Empirical Results**

# _5.1. Baseline Balance and Attrition_

In Tables 2a and 2b, we use baseline data to confirm that household, school, and child characteristics are balanced across the treatment groups and between treatment and control. We first present variable means measured at baseline for the control group and each of the treatment arms. In column 6, we estimate regressions of each characteristic on CCT and UCT treatment dummies, as that is the focus of this paper, and then calculate a Wald test of the equality of the UCT and CCT variables. In column 7, we estimate regressions of each characteristic on dummies for the five groups and then calculate an F-test of the joint test that the means of the five groups are equal. In Tables 2a and 2b, results show good balance overall across study arms for school, 15
household, and child characteristics. In particular, school quality (graduation rates) and resources (provides meals, has latrines, water source, facilities for hand washing, and sufficient chalk and other teaching materials) appear to be consistent across groups. For only one variable (ethnic group is Nankana) is there a statistically significant difference between the CCT and UCT treatments. Across the five groups, we observe statistically significant differences for child age and the proportion of low ability children. While these three significant differences across the 72 tests are likely the product of chance and do not invalidate our identification, our main results are robust to including household level controls and child age and gender in the regressions.

Household attrition was extremely low between the baseline and one-year follow-up survey (1.26 percent), and increased slightly when comparing the baseline and two-year followup survey (3.56 percent). In Table 3a, we explore the relative differences between attritor and non-attritor households. Columns 1 presents means of household-level characteristics from the baseline survey for the sample of households that were followed from the baseline to the twoyear follow-up survey (non-attritors). Column 2 presents means for the sample of attritor households, and column 3 presents the average difference in characteristics between attritors and non-attritors, as well as whether the difference is statistically significant. Results suggest attrition is not likely random, as attritor households are more likely to be smaller and Christian and less likely to be polygamous, animist, or of the Nankana ethnicity. However, what is more relevant for our analysis is whether the attritors’ characteristics differ across treatment and control groups. In column 4, we show the coefficient for the interaction term from a difference-in-differences regression for each characteristic comparing the difference between attritors and non-attritors in the CCT treatment group with the same difference between attritors and non-attritors in the control group. Column 5 presents the corresponding interaction term from a difference-in16
differences regression comparing the UCT and control groups. Across the 32 regressions, we find no statistically significant difference in 30, while we find differences between the CCT and control groups in terms of polygamy and whether the household’s religion is animism.

Table 3b presents a similar attrition analysis for child level variables. Across most characteristics (with the exception of math test scores), children from attritor and non-attritor households look similar. In comparing whether the characteristics of attritors differ across groups, we find no statistically significant difference in 23 of the 26 cases. We find differences between the control group and the intervention groups in terms of child age (both CCT and UCT) and parental self-reports of enrollment (CCT). This last result suggests that differences in selfreports of enrollment between attritors and non-attritors are not similar across control and treatment groups and justifies our attrition-related robustness checks discussed in Section 5.5. _5.2. Impacts on Enrollment_ To analyze the impact of cash transfers on school enrollment, we use two measures of enrollment as dependent variables. The first comes from parental self-reports in the household survey. The second comes from school administrative ledgers we collected at each school. By using two measures, one collected at the household-level and potentially prone to self-reporting bias as highlighted by Baird and Özler (2012) and one collected at the school-level and potentially more objective, it reinforces the robustness of our analysis. The correlation between the parental selfreport and the school-based measure is 0.79.

In Table 4, we analyze the impact of cash transfers on enrollment for all children ages 7 to 15 using the three specifications in Equations 1-3. The Equation 1 specification uses only the round 3 cross-sectional data and relies on the random allocation of interventions but does not control for potential residual baseline variation. For the parental self-report measure (column 1), 17
we find that only the CCT intervention has a positive and significant impact, and we reject equality of the CCT and UCT coefficients. However, using the school-based enrollment measure (column 4), we find positive and significant impacts for both the CCT and UCT interventions and no statistical difference between the coefficients.

In Table 4 (columns 2 and 5), we present results using the Equation 2 difference-indifference strategy. As previously discussed, results show no impact of the conditional or unconditional transfers at round 2 for school year 2008-2009, the program’s first year, because the transfers were delivered too late in that school year. However, the results show significant impacts of transfers at round 3 for school year 2009-2010, when the transfers were delivered on time. More precisely, columns 2 and 5 show significant positive impacts in the CCT villages for children ages 7 to 15, using both enrollment measures, while there is a positive but not significant coefficient for the UCT villages. At round 3, the CCT and the UCT coefficients are significantly different from each other using the self-reported but not the school roster measure. These results are confirmed in columns 3 and 6 when we use the Equation 3 difference-indifference specification using only the baseline and last follow-up surveys (rounds 1 and 3).<sup>23</sup> Overall, when looking at all school-age children, across the two measures of enrollment and the three alternative specifications, Table 4 allows us to conclude that the cash transfer intervention had no impact on school enrollment in the first year (2008-2009), but CCTs had a positive impact on enrollment in the second year. The impact of the UCT intervention on enrollment for all children is less clear and often not statistically significant. The remainder of our analysis extends our discussion of Figure 1 to investigate how the impacts of the conditional and unconditional cash transfers vary with the type of child.

> 23 The point estimates in columns 1 and 4 are larger than in the difference-in-difference specifications in the other columns suggesting that controlling for residual baseline variation is important.

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In Table 5, we explicitly test our “marginal” child hypothesis that UCTs and CCTs would have similar positive effects increasing enrollment for children who are traditionally more likely to go to school, but CCTs are more effective at getting parents to invest in children they normally do not prioritize. We test this hypothesis by examining the impact of the two types of transfers on school enrollment for marginal and non-marginal children, as defined by their baseline enrollment status, gender, age, and cognitive ability. We focus our analysis on the more objective and reliable school-based measure of enrollment and on the Equation 3 specification, a difference-in-difference regression using the baseline and second follow-up surveys.<sup>24</sup> This specification acknowledges the absence of round 2 impacts and focuses on the round 3 impacts. Columns 1 and 2 in Table 5 compare the impacts of the different types of transfers for children who were already enrolled at baseline (column 1) and those who were not enrolled at baseline (column 2). All else equal, children not initially enrolled can be considered more marginal. Both types of transfers lead to positive and significant increases in enrollment for both types of children. Yet while the UCT and CCT coefficients are similar and not significantly different from each other for children enrolled at baseline, the CCT coefficient is significantly larger than the UCT coefficient for children who were not initially enrolled. Thus, CCTs seem to outperform UCTs in bringing into school children who had not been enrolled.

In columns 3-4 of Table 5, we compare the impact of conditional and unconditional cash transfers for boys and girls aged 7 to 15. For boys, CCTs and UCTs have a similar impact in magnitude, positively increasing enrollment by around 11 percentage points. In contrast, for girls

> 24 Baird and Özler (2012) suggest that self-reported enrollment is often overstated and recommend collecting schoollevel administrative enrollment data. In our survey, when comparing parental self-reports and school administrative data, we find that 11.4 percent of all children reported by their parents to be enrolled are not enrolled according to the school data. Appendix Table 1 provides a qualitative summary of the main enrollment results using the parental reports and school-level administrative data. As discussed below, results are consistent with both data sources. Appendix Table 2 presents results using the parental self-reports. Appendix Table 3 includes the other empirical specifications for the school-based data for all the sub-categories analyzed in Table 5 with consistent results.

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only CCTs have a statistically significant positive impact, increasing enrollment by 9.2 percentage points, and we can reject equality between the CCT and UCT coefficients. Since girls are on average less likely to be enrolled at baseline (see summary statistics in Table 1b), these results are consistent with our “marginal” child hypothesis: CCTs and UCTs are similarly effective in increasing the enrollment of children that are more likely to go to school (boys), but CCTs are more effective in increasing the enrollment of more marginal children such as girls.

In columns 5-6, we focus on the differential program impacts by age group. As shown in Table 1b, children ages 9 to 13 form the core school-going population with a higher proportion of children enrolled. Enrollment is lower at ages 7 and 8 as starting school late is typical in rural areas.<sup>25</sup> Unconditional and conditional cash transfers have similar positive impacts for children ages 9 to 13. Only the CCT coefficient is significantly different from zero, but the CCT and UCT coefficients are of similar magnitude and the p-value indicates we cannot reject equality. In contrast, for younger children ages 7 to 8 who are traditionally less likely to be enrolled, CCTs have a significantly larger positive impact than UCTs (column 6).

Columns 7-8 in Table 5 compare the impacts of CCTs and UCTs for higher and lower ability children as measured by the child’s Raven raw score. We define higher ability children as those who have a baseline Raven’s score above the sample mean 6.1 (column 7). Lower ability children are defined as those who have baseline Raven’s scores of 6 or below (column 8). The Table 1b summary statistics and earlier work analyzing the baseline data (Akresh, Bagby, de Walque and Kazianga, 2012a, 2012b) indicate that lower ability children are less likely to be

> 25 Consistent with other CCT programs, the Burkina Faso government decided to provide larger transfer amounts to older children ages 11-15 and smaller amounts to younger children ages 7-10. Our marginal child analysis deviates from those specific age cut-offs because we believe the youngest aged children (7-8) are more marginal due to delayed school enrollment and children ages 14-15 show sharp declines in enrollment because most rural villages do not have access to secondary schools. Nevertheless, our marginal child results are still consistent (results not shown) if we use the government age cut-offs to define marginal and non-marginal children. Further, results (not shown) are also consistent using slightly different age groupings for either the older or younger groups.

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enrolled. Results show that both CCTs and UCTs have a positive impact on enrollment for more able children, and we cannot reject the equality of the coefficients. For lower ability children, both UCTs and CCTs have a positive impact in improving their enrollment, but the effect of CCTs is larger than UCTs (17.4 vs. 9.2 percentage points, equality of coefficients rejected). The results again confirm our marginal child hypothesis suggesting conditionality plays a critical role in ensuring that children who are not normally prioritized for school are now being enrolled.

Appendix Table 1 qualitatively summarizes the Table 4 and 5 results, including the corresponding results using parental self-reports of enrollment (see Appendix Table 2 for the actual parent self-report results). The overall picture, using both enrollment measures, confirms that CCTs have significantly larger impacts on enrollment than UCTs for marginal children such as girls, young children, less able children, and children not enrolled at baseline. The findings are also consistent and robust across alternative empirical specifications (see Appendix Table 3).

In Table 6, we further investigate the differential effects of CCTs and UCTs for subcategories of marginal children.<sup>26</sup> In columns 1 and 2, we divide the sample of young children by gender. For both young boys and girls, CCTs have a statistically significant positive impact on enrollment, and we can reject equality between the CCT and UCT coefficients in both cases. In columns 3 and 4, we divide the sample of less able children by gender. CCTs have a larger impact than UCTs for both lower ability boys and girls, although we only can reject the equality of coefficients for girls (p-value for the test in the boys sample is 0.195). In columns 5 and 6, we divide the sample of less able children by age. For both age groups of low ability children, we find that CCTs have a statistically significant positive impact, but we only can reject the equality of coefficients for the younger group (p-value for the test in the older sample is 0.144).

> 26 Results (not shown) using the two alternative empirical specifications lead to similar conclusions.

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In Table 7, we present robustness checks in which we vary the Raven’s score cut-offs used to categorize children as low or high ability.<sup>27</sup> Raven’s scores ranges from 0 to 18. In Table 5, we use the sample mean of 6.05 as the threshold, with lower ability children defined as those with scores between 0 to 6 and higher ability children those with scores between 7 to 18. We reproduce those results in column 3. In the other Table 7 columns, we decrease and increase the ability cut-off to verify that our results do not depend on the chosen cut-off. We find that for low ability children, CCTs consistently outperform UCTs irrespective of the ability threshold used. _5.3 Impacts on Attendance_ In Table 8, we analyze the impact of cash transfers on school attendance rates of all children ages 7-15, unconditional on their enrollment. This is a broad measure of school participation with direct policy relevance that accounts for enrollment and attendance effects and is not confounded by changes in the share of the sample enrolled. We rely on attendance taken from school ledgers collected at each school.<sup>28</sup> For each child, we compute the percentage of school days attended for the entire academic year. Children who are not enrolled receive an attendance rate of zero. The attendance results are consistent with the marginal child hypothesis described for enrollment.<sup>29</sup> CCTs increase school attendance at round 3 for all children and in all subgroups. UCTs increase attendance for non-marginal children (those enrolled at baseline, boys, older children, and higher ability children). For marginal children (those not enrolled at baseline, girls, young children, and low ability children), CCTs significantly outperform UCTs as we can reject the equality of the coefficients, while we cannot reject that equality non-marginal children.

> 27 Results (not shown) using the two alternative empirical specifications lead to similar conclusions. 28 We also collected parental self-reports on attendance for the two weeks prior to the survey and so the results are not directly comparable with the school-based data. Moreover, since some villages were surveyed after the end of the school year, this self-reported measure is potentially less-reliable. Nevertheless, the analysis using parental selfreports of attendance yield results similar and consistent with the Table 8 results.  .

> 29 Similar results using the other empirical specifications are presented in Appendix Table 4.

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# _5.4 Impacts on Learning Outcomes_

Table 9 measures impacts of the two different types of cash transfers on learning. We examine scores on a standardized mathematics and French test (French is the official language in Burkina Faso and the language used in all primary schools), which were designed by the survey team in collaboration with education specialists at the Burkina Faso Ministry of Education. The tests were given to all children ages 7 to 15 in the surveyed households. We examine the impacts separately for enrolled children (as indicated by the school data) and for all children. We also examine impacts on final end-of-year school grades (column 1). Unlike the tests we designed for French and mathematics, final grades are only available for enrolled children. They are also not standardized and can thus vary across schools or even within schools. In columns 2 and 5, the dependent variable is the age-standardized z-score for the number correct on the mathematics test. In columns 3, 4, 6, and 7, the dependent variables are age-standardized z-scores for the number correct on the overall French test and the French reading sub-section, respectively.

We find no significant impact of the interventions on grades or achievement tests, except for a positive impact of CCTs on the reading section of the French test for the sample of all children.<sup>30</sup> However, it is important to stress that even though there is no differential learning across treatment and control groups, this does not mean there is no learning going on for these children. For children in the treatment groups who get enrolled between baseline and round 3, their mean test scores increase and they improve at the same rate as for children in the control group who get enrolled across rounds. Our findings imply that transfers increase enrollment, and these children (who would not have enrolled absent the intervention) are learning as much as their peers in the control group. This can further be seen by comparing the results for all children with only enrolled children. For all children, the coefficients tend to be positive (especially for

> 30 Results (not shown) using the two alternative empirical specifications lead to similar conclusions.

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the CCTs) although not statistically significant and they are larger for the full sample (columns 5-7) than the restricted sample of enrolled children (columns 2-4). This suggests that in the overall population of children learning increases as more children are enrolled. In the sub-group analyses by gender, age, and ability level (results not shown), most coefficients are not significant. Overall, it is fair to conclude that the impacts on learning are limited, which is consistent with results for most other cash transfer programs (Filmer and Schady, 2009 and Benhassine et al., 2012 also find limited learning impacts in Cambodia and Morocco, respectively, but Baird, McIntosh, and Özler, 2011 document positive learning in Malawi). _5.5 Robustness Checks: Attrition and Selection_ Tables 10 and 11 include robustness checks related to attrition and selection for the analyzed samples. In Table 10, we investigate with child-level regressions whether the child’s household was resurveyed in round 3 (column 1), whether the child’s enrollment or attendance information was missing from the school roster (columns 2 and 3), and whether the child did not take the mathematics and French achievement tests (column 4). We do not find any evidence that the treatment groups are correlated with household attrition, missing child information in the school rosters, or missing achievement tests.

While those results are reassuring and while attrition in our sample is low, to further confirm that attrition does not significantly impact our findings, in Table 11, we re-estimate regressions adjusted for attrition using an inverse probability weighting (IPW) approach suggested by Wooldridge (2002, 2010). IPW is based on the key assumption that sample attrition is ignorable with respect to the dependent variable, conditional on the observables in the attrition equation (Wooldridge, 2002). The IPW procedure consists of two stages. First, data from the baseline round are used to estimate the probability a household remains in the survey in round 3.

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The inverse of the predicted probabilities are then used to weight the data, essentially giving more weight to households who are more likely to leave, conditional on observables. The results of the IPW regressions in Table 11 are consistent with the results on all children (columns 3 and 6 of Table 4) and on marginal children (columns 2, 4, 6, and 8 of Table 5).

# _5.6 Cost-effectiveness Analysis_

In Table 12, we compare the program impacts to its costs. The cost estimates in columns 1 and 2 include only the cash transfers given to households. Columns 3 and 4 include the administrative costs as well as the cash transfers. On average, each child received $13 per year under UCTs and $9 per year under CCTs (columns 1 and 2).<sup>31</sup> Including administrative costs, UCTs cost about $22 per child per year whereas CCTs cost about $20 per child per year.<sup>32</sup> Administrative costs are large relative to intervention costs, but this is common for pilot projects for which there are no economies of scale<sup>33</sup> . Given the size of the cash transfers and the estimated program impacts, we estimate how much it would cost to enroll one additional child. We also disaggregate our cost-effectiveness estimates by gender, age, and child ability.

It costs less to enroll an additional child under CCTs than under UCTs. If we consider transfer costs only (columns 1-2), enrolling an additional child ages 7 to 15 for one year requires $89 under CCTs and $194 under UCTs. The gender difference is more pronounced under UCTs than CCTs. Under UCTs, enrolling an additional girl costs $458 or 4 times more than enrolling an additional boy ($116), whereas under CCTs enrolling a girl costs 1.2 times more than

> 31 We report total transfers distributed divided by the number of eligible children in the treatment households. Hence for CCTs, the average amount actually received would be higher for children who satisfied conditionality. 32 In this small scale pilot, the administrative costs of verifying conditionality in the CCT villages were low because the government relied on existing committees of village volunteers. Therefore, administrative costs raised the total program costs only marginally more for CCTs than UCTs. Such an arrangement might not be feasible in all settings. 33 Caldés, Coady and Maluccio (2006) document cost-to transfer ratios (CTRs) for three programs in Latin America. Over the length of the programs, they find CTRs of 10.6 percent in Mexico, 49.9 percent in Honduras and 62.9 percent in Nicaragua. For the first year of the programs, the CTRs are 134.2, 114.5 and 254.3 respectively.

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enrolling a boy.<sup>34</sup> Under CCTs, enrolling one additional child ages 7 to 8 costs $37 per year, which is less than the $94 it costs to enroll one additional child ages 9 to 13. Similarly, CCTs cost less to enroll an additional low ability child ($51) than a high ability child ($61). In contrast, enrolling an additional low ability child under UCTs costs $139, 1.7 times the amount needed to enroll an additional high ability child. Overall, the estimates indicate that CCTs are more costeffective at improving enrollment, particularly for marginal children that parents would not have enrolled. Accounting for administrative costs (columns 3-4) does not alter the overall pattern. Given the higher administrative costs for CCTs, it is noticeable that CCTs remains more costeffective even after we account for these administrative costs.

One way to compare UCTs and CCTs would be to consider the hypothetical scenario where all resources are shifted from UCTs to CCTs. This corresponds to dividing column 1 by 2 or column 3 by 4. For all children, the cost per additional enrollment under UCTs would be 2.2 additional enrollments under CCTs, or to 1.7 additional enrollments when administrative costs are accounted for. The gains from reallocating resources from UCTs to CCTs are even larger when considering marginal children. For girls, the gain is about 4.8 and 3.7 additional enrollments, with and without administrative costs, respectively. For young children, the corresponding figures are 3.7 and 2.9, while for low ability children, the change is 2.8 and 2.1. We also compare our program’s impacts with other programs with similar objectives. Such a comparison is made difficult not only by the fact those programs took place in different contexts and countries, but also because programs often have multiple objectives and should not be judged solely on school enrollment impacts. With these caveats in mind, our CCTs have comparable enrollment impacts to the mid-range of cost-benefit estimates from other studies,

> 34 Note that, the estimated impact of UCTs is small in magnitude and not statistically different from zero for girls. Therefore, it is plausible that $458 would not get one additional girl in school.

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including school meals in Kenya at $43.34 (Vermeersch and Kremer, 2005) and teacher incentives in India at $67.64 (Duflo, Hanna and Ryan, 2012). However, the costs to enroll an additional child are higher than cheaper interventions such as deworming in Kenya at $4.36 (Miguel and Kremer, 2004). On the other hand, the cost per additional child enrolled is substantially lower compared to other CCT programs. de Janvry and Sadoulet (2006) estimate the Mexican Progresa program cost $9600 for each additional primary school enrollment. They demonstrate that efficiency gains through better targeting mechanisms could reduce this cost to $802-$1151, which would still be significantly larger than our cost estimates.

# **6. Conclusion**

Social safety nets are actively promoted in developing nations both as responses to financial crises and as mechanisms to alleviate poverty. Conditional cash transfers, which are now common in Latin America but remain rare in other regions, are also seen as a way to reduce future poverty by investing in the next generation’s human capital (Fiszbein and Schady, 2009), but the role of conditionality in achieving this objective is unclear. In this paper, we explicitly compare the impact of conditional and unconditional cash transfers on schooling outcomes in the same environment using a randomized experiment in rural Burkina Faso. Our results indicate that UCTs and CCTs have similar impacts increasing the enrollment of children who are traditionally prioritized by households for school participation such as boys, more able children, and those of core school-going age. However, CCTs are more effective than UCTs in improving the enrollment of “marginal” children, those who are initially less likely to go to school, such as girls, lower ability children, and younger children. Results are consistent with the literature on compensating versus reinforcing investments that finds parents often decide strategically to invest more in the education of some of their children (Behrman, Rosenzweig and Taubman, 27
1994; Bharadwaj, Loken and Neilson, forthcoming; Akresh and Edmonds, 2011; Almond and Currie, 2011; Adhvaryu and Nyshadham, 2012).

Our results shed new light on the role of conditionality in cash transfer programs, by suggesting how and for which categories of children CCTs outperforms UCTs. In resource-poor settings, both UCTs and CCTs relax the budget constraint and allow households to enroll more of the children they would traditionally prioritize for human capital investments. But the conditions attached to CCTs play a critical role in improving the outcomes of children for whom parents are less likely to invest.

The policy implications of those results are clear: the choice between CCTs and UCTs should be influenced by the objectives of the education policy. If the objective is to increase overall enrollment, UCTs might have comparable effects to CCTs. Since CCTs programs are generally significantly more costly to administer per recipient than UCT programs, due to the expenses associated with monitoring that the conditions are met, UCTs are generally assumed to be more cost-effective under that objective. However, this is not that what we found in this study. Furthermore, if the policy objective also includes an emphasis on improving the enrollment and educational outcomes of categories of children who are less likely to be part of the education system, then CCTs are likely to have larger impacts and be more cost-effective. That conclusion is especially relevant in the context of Millennium Development Goal 3 which focuses on reducing the gender gap in education.

From a policy-making perspective, our study also addresses the feasibility of conditional cash transfer schemes in Sub-Saharan Africa. Since CCT programs rely on a certain level of administrative capacity (the ability to target households, plan meetings to notify households of their obligations and rights, monitor household compliance and conditionality, and transfer funds 28
to families), there is a debate on whether these programs, which have been successful in Latin America, can be successfully implemented by African central or local governments (Samson, 2006; Schubert and Slater, 2006; Szekely, 2006; Freelander, 2007). The cash transfer program we study relied on existing government structures and was implemented in an environment where there is no systematic population registration and where formal banking is almost nonexistent. Even though our study was a two-year pilot limited to one province and its scalability remains to be investigated, it nevertheless indicates that CCTs can be implemented and be effective in an environment with limited administrative capacity.

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