EVALUATION OF THE IMPACT OF A PILOT-PROJECT OF CONDITIONAL AND UNCONDITIONAL
CASH TRANSFERS IN THE NAHOURI PROVINCE OF BURKINA FASO
CONCEPT NOTE
1. Introduction
The project’s goal is to use a randomized experimental design to evaluate the impact and
compare the effectiveness of four resource transfer programs to poor households in developing
countries: conditional cash transfers given to the mother, conditional cash transfers given to the
father, unconditional cash transfers given to the mother, and unconditional cash transfers given
to the father. The study will compare the interventions’ educational, health, and early childhood
development impacts in Nahouri province in southern Burkina Faso from 2008 to 2011.
Conditional cash transfer (CCT) programs have become one of the most popular social
sector interventions in developing countries. While the program design details vary, all programs
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, taking them for
regular health care visits, and receiving necessary immunizations). CCT programs have two clear
objectives. First, in making transfers conditional, the program seeks to encourage human capital
accumulation and break a vicious cycle in which poverty is transmitted across generations.
Second, the program attempts to provide poor households with a consumption floor and to
improve a household’s asset base and income generating potential. A growing number of
countries, in particular in Latin America, but also in Asia have implemented such programs.1 In
Africa, two CCT pilot programs (in South Africa and Kenya) have been implemented, but both
focus exclusively on orphans and HIV households and neither has yet been rigorously evaluated.
1
As of 2007, the following countries in Latin America have implemented CCT programs: Argentina, Brazil, Chile,
Columbia, Dominican Republic, El Salvador, Honduras, Jamaica, Mexico, Nicaragua, Paraguay, and Peru, while
these Asian countries have started CCT programs: Bangladesh, Cambodia, Mongolia, Pakistan, and Turkey.
1
The CCT programs contrast with unconditional cash transfer (UCT) programs, which do
not impose conditionality constraints. There are two main differences between UCT and CCT
programs. First, CCT programs represent a “top-down” approach in which the outside authority
decides what is best for poor children and provides incentives to their parents to achieve these
objectives. On the other hand, UCT programs assume that parents, once the income constraint is
removed, are in a better position to make appropriate decisions regarding their child’s health and
education. Second, CCT programs are significantly more costly to administer than UCT
programs, due to the expenses associated with monitoring that the conditions are met. While
there have been previous randomized evaluations of CCT programs in several Latin American
countries and non-randomized evaluations of UCT programs, there have been no rigorous
evaluations of these two transfer schemes within the same local environment, an exercise that
would enable policy makers and researchers to compare the benefits and costs of each approach.2
The proposed impact evaluation is designed to answer at least four critical policy
questions related to social protection programs in developing countries.
1) Can CCT programs, which have been shown to be effective in Latin America, be
effective in 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 to families), can these
programs be successfully implemented by African central or local governments?3
Skoufias (2005) provides an overview of the program evaluations conducted for Mexico’s CCT program, Progresa,
while Maluccio and Flores (2005) provide a summary of the program evaluations for Nicaragua’s, Red de Proteción
Social. Devereux, Marshall, MacAskill, and Pelham (2005) provide a qualitative evaluation of 15 UCT programs in
eastern and southern Africa.
3
The cost of administrative capacity is also significant. Caldes, Coady and Maluccio (2006) estimate that for the
CCT program in Honduras, Programa de Asignación Familiar, $0.50 of program costs are spent for every $1 of
transfers given to households, while for Nicaragua’s CCT program, $0.63 of program costs are spent for every $1 of
household transfers. Mexico’s CCT program only incurred $0.11 of program costs for every $1 of transfers.
2
2
2) Are CCT programs effective mainly because of the cash transfers or because of the
conditionality? Our project will compare conditional cash transfers with unconditional cash
transfers, which permits researchers and policy makers to determine whether it is the additional
income or the explicit incentive mechanism that leads to the CCT program impact. While this
question continues to be debated, no randomized evaluations comparing CCT and UCT
programs have yet been conducted.
3) Does the gender of the transfer recipient influence the program’s impact? We will
examine the potentially differential impacts resulting from giving cash transfers to mothers
versus fathers. Numerous intrahousehold bargaining research papers indicate resources under the
mother’s control have a stronger positive impact on a child’s health and schooling than when
those resources are controlled by the father.4 However, almost all current cash transfer programs
give the resources to the mother, so it is not possible to disentangle how much of any impact is
due to the recipient’s gender, how much is due to the income effect, and how much is due to the
change in relative prices associated with the conditionality. Furthermore, the recipient’s gender
might impact outcomes differently for conditional as opposed to unconditional cash transfers.
4) Do these cash transfer schemes have different impacts on asset accumulation, riskcoping, consumption, and production decisions? For a program to break the intergenerational
transmission of poverty, in addition to investments in a child’s human capital and health, it must
also help households get out of long-term poverty traps that are often linked to insufficient
household assets (Carter and Barrett, 2006). The regularity and size of the cash transfers might
remove liquidity constraints allowing the household to improve its asset holdings and short-run
income generating activities. It might also lead to increased consumption due to improved risk4
Influential papers by Schultz (1990), Thomas (1990), and Lundberg, Pollak, and Wales (1997) provide empirical
evidence supporting this finding. For a recent overview of the intrahousehold bargaining literature see Strauss and
Thomas (1995); Haddad, Hoddinott, and Alderman (1997); and Strauss, Mwabu, and Beegle (2000).
3
coping strategies and production increases due to the use of modern inputs. However, UCT and
CCT programs, due to the conditionality restrictions of the CCT program, could yield different
impacts on asset accumulation, consumption, and production outcomes.
From a policy perspective, the answers to these four questions are crucial to help design
cost-effective programs to help break the intergenerational transmission of poverty in developing
countries.
2. Program Intervention and Research Objectives
Cash transfer schemes represent a substantial fraction of the intervention portfolios of
development institutions such as the World Bank, and the population of individuals reached, as
well as the resources used, has surged during the last 5 years. Given this, the need for
randomized evaluations measuring the impact of UCT programs and comparing different types
of cash transfer programs in the same environment is all the more imperative. Further, the gap in
our knowledge of how the gender of the transfer recipient interacts and influences child and
household outcomes also needs to be filled. Using a randomized experimental design, the
project’s objective is to compare the impact of conditional and unconditional cash transfers and
examine the role of the program recipient’s gender in influencing outcomes.
The study will take place in Nahouri province in southern Burkina Faso. For several
reasons, Burkina Faso offers a useful setting for evaluating these interventions. First, educational
achievement and child health indicators are low in Burkina Faso, so these programs could benefit
a large number of children. Second, the Burkina Faso government has agreed that, at the study’s
conclusion, the recommendations from the program evaluation will be utilized to determine
which social protection program to expand to the rest of the country.5
5
Within Burkina Faso, there are currently fewer interventions targeting Nahouri province, which will help minimize
any confounding effects that could be induced by the presence of other development programs.
4
The evaluation will be based on the analysis of longitudinal household surveys combined
with health facility, primary school, and village surveys. A baseline household survey took place
in May-June 2008 before the intervention started in October 2008 (at the onset of the 2008-2009
academic school year). There will be follow-up surveys in May-June 2009 and May-June 2010,
allowing sufficient time for potential program impacts to accumulate.6
In addition to the program’s direct impact on education and health outcomes, the study
will also explore other direct effects of cash transfers. By providing households with a steady
cash flow and a consumption floor and by removing liquidity and credit constraints, cash
transfers can influence household production both on and off-farm. For instance, households
might adopt production technologies they would not have otherwise adopted or take additional
risks to improve farm productivity and output (Dercon and Christiaensen, 2007). By increasing
the income level within the community, cash transfers can generate multiplier effects beyond the
primary outcome of interest (Gertler, Martinez, and Rubio, 2005). These programs might also
generate significant spillover effects within the communities even for households that did not
receive treatment interventions (Angelucci and De Giorgi, 2006). Our sample design as well as
the survey instruments will ensure that we can explore these questions in detail.
Evaluations of CCT programs in Latin America provide evidence of their ability to
positively influence both educational and health outcomes of children in poor households in a
6
The household survey is similar to a Living Standards and Measurement Survey as detailed by
Grosh and Glewwe (2000) with extensive education and health modules. The survey also covers
early childhood development outcomes and collects individual and household characteristics that
may influence the intervention’s impact. We are collecting a lot of child related information at the
household level: school enrollment, school attendance, anthropometrics, child labor and domestic chores, health
indicators, cognitive ability, achievement tests. We are also trying to raise additional funds to add biomarkers such
as anemia for the 2nd and last follow-up survey in 2010.
The village, school, and health facility surveys are based on those used in the Progresa evaluation and enable
measurement of variables that may impact the transfer programs. Appendix 1 contains further details concerning the
survey modules.
5
relatively short time period.7 However, conditionality greatly increases the program cost and the
necessary level of government involvement and administrative capacity. These increased costs
and administrative needs have led to the argument that CCT programs are well suited for middleincome countries but cannot be implemented in low-income African countries with weak
administrative capacities (Samson, 2006; Székely, 2006; Freelander, 2007). This argument is
part of a broad debate on which circumstances are appropriate or necessary for using a particular
intervention scheme (de Janvry and Sadoulet, 2005, 2006).
In contrast to CCT programs, unconditional cash transfers to poor targeted households
are less costly (as there is no need to enforce conditionality) and evidence demonstrates their
effectiveness. An evaluation by Case, Hosegood, and Lund (2005) of the South African Child
Support Grant, an unconditional cash transfer targeted to families with young children, finds a
large positive schooling impact, while Aguero, Carter, and Woolard (2006) evaluate the same
program and find an improvement in children’s nutrition. Evaluations of South Africa’s pension
program (a type of unconditional cash transfer) show an increase in school enrollment and
improvements in children’s health (Case and Deaton, 1998; Duflo, 2003; Edmonds, 2006).
However, none of these UCT program evaluations were randomized, which yields the possibility
that unobservable factors correlated with receipt of the treatment also influence outcomes.
For a UCT program in Ecuador that incorporated an explicit randomized evaluation,
results show significant positive improvements for schooling (Araujo and Schady, 2006) and
nutritional status and cognitive development (Paxson and Schady, 2007). However, in the
implementation of the UCT program, program administrators stressed the importance of
7
See Behrman, Cheng, and Todd, 2004; Gertler, 2004; Hoddinott and Skoufias, 2004; Schultz, 2004; Attanasio et
al., 2005; Behrman and Hoddinott, 2005; Bobonis and Finan, 2005; Maluccio, 2005; Olinto, Shapiro, and Skoufias,
2005 for these evaluations. Evidence also suggests that conditional cash transfers help protect children’s schooling
from negative household income shocks (de Janvry, Finan, Sadoulet, and Vakis, 2006).
6
schooling, which led some households to believe that conditionality was part of the cash transfer.
In addition, 42 percent of households in the control group received cash transfers, raising doubts
about the randomized evaluation design (Schady and Rosero, 2007).
Several recent studies attempt to directly compare CCT and UCT programs. De Janvry
and Sadoulet (2005) present theoretical arguments for why a CCT program should have a larger
impact on the conditioned outcomes than a UCT program. Kakwani, Soares, and Son (2005)
present ex ante simulations arguing that UCT programs will have a small impact in Africa.
Finally, for some CCT recipients in Mexico’s Progresa program, the conditionality requirements
were not enforced and results show educational attainment was reduced (for these pseudo-UCT
households) but only for students transitioning from primary to secondary school (de Brauw and
Hoddinott, 2007).
One of the literature’s main gaps is the lack of a rigorous, randomized evaluation of both
CCT and UCT programs within the same local environment. This comparison is not only of
academic interest. African policy makers do not know if CCT programs are feasible given the
administrative constraints they face, and they do not know if UCT programs, by removing a
constraint the households face, will achieve the desired improvements in children’s schooling,
health, and early childhood development, as well as reduce household poverty and improve asset
accumulation. By being the first to provide a comparison of the impact of a CCT and UCT
program within the same local environment, the findings of this project will help development
practitioners determine the most effective ways to transfer resources to the poor.
Characteristics about who receives the cash transfer, in particular the recipient’s gender,
might have significant impacts on how the transfer income is used and the subsequent program
impact. Non-unitary household bargaining models predict that cash transfers given to mothers
7
will increase their bargaining power within the household and lead to expenditures that better
reflect the mother’s preferences (Chiappori, 1988; Lundberg and Pollak, 1993). However, a
significant difficulty in the intrahousehold bargaining literature to empirically prove this point is
the potentially endogenous nature of men’s and women’s income. To solve this problem, we
randomly allocate cash transfers to either the mother or the father. Almost all existing cash
transfer programs provide the resources only to the mother, making it impossible to determine
how much of any impact is due to the recipient’s gender, how much is due to the income effect
and how much is due to the change in relative prices associated with the conditionality.
Decision-makers face challenges and trade-offs when designing social assistance
programs. Targeting and conditionality may increase effectiveness and maximize impact but
generating information to set targeting rules and monitoring conditionality rules can be costly.
Administrative burdens created by enforcing conditionality might limit the ability of low-income
African nations to implement widespread CCT programs. A rigorous, randomized evaluation can
provide the magnitude of the short-run impact and cost under each transfer scheme. By using
household behavioral models in addition to the mean comparisons across treatment and control
groups, the results will provide a benchmark of the resource amount required for a desired
impact level, given local population characteristics and a particular intervention scheme.
3. Evaluation Design and Data Collection
3.1. Program Structure and Sampling Design
The research protocol consists of randomly assigning 3250 households in 75 villages to the
following five groups (with 650 surveyed households in each group): (i) conditional cash
transfers given to the father, (ii) conditional cash transfers given to the mother, (iii) unconditional
8
cash transfers given to the father, (iv) unconditional cash transfers given to the mother, and (v) a
control group.8
We were limited to 75 villages for political and budgetary reasons. The Government of
Burkina Faso did not want to pilot the project in more than one province, mainly for budgetary
reasons and we had to work in one of the Provinces where the Bank HIV/AIDS project was
active. That limited our choice. We have 75 villages because we took all villages in the Province
with a primary school in a 5km radius. We reasoned that it did not make sense to conduct a study
about a demand-side education intervention where the supply of education is inexistent.
While 15 villages per evaluation group is limited, we have just completed an impact
evaluation of school feeding programs in Burkina Faso and we found significant effects after one
year of intervention with evaluation groups of 15 villages on average. (Kazianga, de Walque and
Alderman, 2009). In this experiment, we will have 2 years of intervention, so we are fairly
confident that we will be able to detect potential effects.
We have recently conducted a preliminary analysis of the baseline data collected in MayJune 2008 and we found that the sample was well balanced across the four intervention groups
and the control group on a large range of individual and household characteristics, indicating that
the randomization appears to have worked well.
Only poor households are eligible to receive a cash transfer (below we discuss in detail
the targeting of how households are divided into poor and non-poor groups).
Within the four cash transfer groups (60 villages), we interview three types of families.
First, we interview poor households eligible to receive the transfer and who are randomly
8
The 75 villages are all villages in Nahouri province that have a primary school. The project does not address any
potential supply-side constraint issues and therefore results can only be generalized to the universe of villages with a
primary school. Due to the low current primary school enrollment rates in Burkina Faso, the program intervention
focuses exclusively on primary schooling as opposed to covering all grades.
9
selected to receive it. Second, we interview poor households who are eligible to receive the
transfer but are not randomly selected to receive it. Third, we interview non-poor households
who are not eligible to receive the transfer. In each of these four groups of 15 villages (based on
sample size power calculations), we interview 500 poor households randomly selected to receive
a transfer, 75 poor eligible households that did not receive a transfer, and 75 non-poor
households that are not eligible to receive a transfer. Interviewing non-poor households in
villages where some poor households receive a cash transfer allows us to evaluate whether the
infusion of resources to the village has any spillover effects to these non-poor households.
Likewise, interviewing poor, eligible households that did not receive a transfer but live in
villages where other poor households did receive a transfer allows us to measure any spillover
effects to these poor non-recipient households. Finally, the control group consists of randomly
selected households in villages where no households receive cash transfers. In these 15 control
villages, we interview 575 randomly selected poor, eligible households that do not receive a cash
transfer and 75 non-poor, non-eligible households. Figure 1 diagrams the five different groups
and indicates within each village the eligible and non-eligible households to be interviewed.
Since it is not feasible to collect consumption data from every household in a village to
determine poverty status, we use the most recent Burkina Faso nationally representative
household survey to estimate the relationship between household consumption, living structure,
assets, and village characteristics as represented by the equation: c    X   Z    where ci
i
0
i 1
i 2
i
is consumption for household i, Xi represents household housing material and asset ownership,
and Zi represents community level characteristics. We utilize this national relationship and local
household information about living structure, assets, and village characteristics (collected in an
expanded household census we will conduct prior to the baseline survey in each of the 75
10
villages) to calculate a predicted consumption level for each household and compare that with
the national poverty line to determine whether a household is considered poor or non-poor.9
Based on the program evaluation literature, our experience with randomized program
evaluation in Burkina Faso, and qualitative focus groups we conducted in Nahouri province, we
believe that transparency in the randomization process is critical to maintain a household’s
participation in the surveys and to guarantee the local authorities’ support. Hence, the assignment
process of randomly allocating villages into five groups and households being randomly selected
to receive a transfer will be done publicly in front of the villagers and local leaders.10
Each of the four treatment groups will receive equal amounts of resources per capita over
the two-year cash transfer program period. To provide additional incentives, the stipend (CCT or
UCT) will increase with a child’s age because both the opportunity cost of a child’s time and the
direct costs of schooling increase with age. As a consequence, households with different
household composition in terms of children will receive different sums. For each ‘composition’,
this can be seen as a different intervention. We will therefore propose to run the analysis for the
different age groups. For households randomly assigned to a CCT scheme, the mother or father
will receive a monthly stipend for each child, conditional on the child being enrolled in school
and the child’s school attendance being above 85 percent in the previous month. CCT
9
The census recorded information about household living structure (cement or mud brick walls, metal or straw
roof), household asset ownership (bicycle or plough), and village information concerning the presence of a market,
all-season road access, and distance to the province capital, the nearest school, and the nearest health clinic. In
practice, we only used 1 village level variable out of 9 variables to determine household eligibility--and this is
whether the village has a market or not. There is roughly an even split between villages with and without markets
(40% with and 60% without), so this should balance out.
10
In the first stage of the randomization process the 75 villages are randomly assigned to the five groups using a
participatory lottery conducted in the province capital in which each village has two representatives present and a
lottery using numbered balls determines who receives which intervention. In the second stage, in each of the 60
villages that will receive a cash transfer program, all eligible households will be present for a participatory lottery to
randomly assign households to either receive or not receive the particular type of transfer allocated to that village.
Given the transfer program’s limited budget, in consultation with village leaders, we decided that randomization is
the fairest way to determine which eligible households receive a transfer and everyone is aware that not all poor
households will get a transfer during the pilot program.
11
households with children under age five will receive a monthly grant conditional on regular
health clinic visits and vaccinations for their children. For households randomly assigned to a
UCT program, the mother or father will receive a monthly stipend for each child, but there are no
requirements or conditions linked with receiving the stipend and parents are not required to
enroll their children in school. UCT households with children under age five will receive a health
grant but are not required to adhere to scheduled health clinic visits for the child.11
As with any longitudinal survey, sample attrition is a potential concern and could be
problematic if attrition is not random or is associated with the interventions. Previous
longitudinal household surveys evaluating a school feeding program by two of the PIs in Burkina
Faso had a sample attrition rate of less than one percent per year. To minimize child fostering in
response to the program introduction and the subsequent sample attrition, households are eligible
for cash transfers based only on the children present in the household at the time of the baseline
survey. Also, we plan to track any children who move from their baseline households (see
Akresh, 2007 for details on a project tracking foster children in Burkina Faso). Finally, it will be
explained to all households that after the two-year pilot program intervention and evaluation, the
most successful program will be expanded to all eligible households in Burkina Faso and the role
of the control group households is critical to that evaluation.
3.2 Identification
The experimental design allows us to attribute any differences in outcome indicators
(enrollment and attendance rates, test scores and grade progression, child health, BMI, early
childhood development and psycho-social indicators, consumption, asset accumulation) between
the treatment and control groups to the impact of the program. The availability of baseline data
The sampling design and program evaluation have received approval from the Burkina Faso government’s Health
Sciences Research Institute Review Board.
11
12
and the data’s panel dimension can be used to control for initial differences between treatment
and control groups using a difference-in-differences model. Not only will we evaluate direct
program effects on eligible households, but we consider indirect program effects on both eligible
and non-eligible households, yielding a more complete comparison of the interventions.
3.2.1 Direct Program Effects
To evaluate the direct program effect on the treated households, or the Average
Treatment Effect (ATE), we want to measure the difference between the potential outcome (Y1i)
for poor households (Pi = 1) in a treated village (Ti = 1) in the presence of the treatment and the
potential outcome (Y0i) for poor households in a treated village in the absence of the treatment:
ATE  E(Y1i Ti  1, Pi  1)  E(Y0i Ti  1, Pi  1) . However, since we do not observe the potential
outcome for poor households in a treated village in the absence of the treatment, (Y0i), we use the
poor households in control villages (Ti = 0) as the counterfactual. We assume the potential
outcome for poor households in a treated village in the absence of the treatment in the village
would be the same as the potential outcome for poor households in the absence of the treatment
in control villages, E (Y T  1, P  1)  E (Y T  0, P  1) . Therefore, the ATE is given by,
0i i
i
0i i
i
ATE  E(Y1i Ti  1, Pi  1)  E(Y0i Ti  0, Pi  1) , but it could be violated if control communities are
indirectly affected by the program. For example, changes in child labor supply in a treatment
village could potentially impact labor supply in a control village. However, given the lack of
integrated wage labor and credit markets in rural Burkina Faso, this is not a significant concern.
The following equation is estimated to find the ATE for poor households:
Yi   0  1Ti   2 X i   3 Z i   it
(1)
where Yi is an outcome for child i (enrollment status, attendance rate, scores on reading and math
tests, health status, time allocated to household chores), Ti is the treatment indicator, Xi is a
13
vector of child characteristics (gender, age, birth order) and household characteristics (wealth,
parent education and literacy, household shocks) and Zi is a vector of village level characteristics
(village infrastructure, school quality, village social capital)12. The direct impact of the treatment
program on the treated households, or ATE, is measured by 1. Given the multiple interventions,
we will be able to compare the treatment impacts for the treated households across the different
programs (CCT given to the mother or father and UCT given to the mother or father) and to
accurately measure which program intervention had the largest average impact on the treated.
3.2.2 Indirect Program Effects
To evaluate the indirect treatment effect (ITE) on households that did not receive a
transfer but live in treatment villages, we follow a similar methodology as with the direct
program effect. There are two types of potential spillovers: those impacting non-poor households
who are not eligible to receive a transfer but live in a treatment village and those impacting poor
eligible households who were randomly selected to not receive a transfer but live in villages
where some poor households did receive transfers. We assume the potential outcome for nonpoor households in a treated village in the absence of the treatment would be the same as the
potential outcome for non-poor households in the absence of the treatment in control villages,
E (Y0i Ti  1, Pi  0)  E (Y0i Ti  0, Pi  0) . Therefore, the ITE for non-poor households is given by:
ITE  E(Y1i Ti  1, Pi  0)  E(Y0i Ti  0, Pi  0) . The ITE for poor households that did not receive a
transfer but live in treatment villages is similarly derived. Learning the size of the program’s
indirect effect across the transfer schemes and comparing direct and indirect impacts is an
essential strategy as it might yield different overall program evaluations than when looking only
12
All evaluation equations for the average treatment effect (ATE) will use village fixed effects, i.e. controlling for
additive heterogeneity.
14
at the direct treatment effect. In addition, as there are significant costs associated with accurately
targeting poor households due to fielding a detailed census prior to the intervention, it is critical
to know the size of program spillovers to poor households not receiving treatment.
4. Collaboration and Capacity Building
This project is expected to contribute to the long-term training of researchers in Burkina
Faso. Our project team has extensive experience conducting quantitative household surveys in
developing countries, especially Burkina Faso. The team members have strong institutional links
with local institutions including the University of Ouagadougou and the Ministry of Education
and Health.
5. Conclusion
We propose a randomized evaluation design to measure and compare the impact of two
types of resource transfers to the poor (conditional cash transfers and unconditional cash
transfers) and we take into account the gender of the cash transfer recipient by comparing the
impact when the mother or the father receives the transfer. While there have been a number of
conditional cash transfer programs in Latin America and Asia, few have been tried in Africa, and
none in Africa have been rigorously evaluated. In addition, few research projects have tried to
determine the mechanism causing certain types of cash transfer programs to be effective. This
project would be the first to provide a comparison within the same local environment of the
impact of these different transfer schemes and would be able to better understand how much of
any impact is due to income changes, how much is due to changes in relative prices due to
conditionality, and how much is due to the cash transfer recipient’s gender.
The primary objective of the interventions is to improve children’s health, schooling and
early childhood development outcomes. However, a consistent cash flow to households also
15
reduces income risk and credit constraints, two key impediments to improving household asset
accumulation and production. This could have far-reaching effects on current poverty reduction,
in addition to the intergenerational transfer of human capital and improved health.
The project will yield significant benefits beyond those to the treatment households.
Because of the randomized evaluation design and our baseline measurement of initial conditions
at the village and household levels, our findings can be generalized to other regions of Burkina
Faso and other developing countries. In addition, extensive host country capacity building (both
formally and informally) will provide researchers and policy makers with skills and training to
conduct further program evaluations of other development projects.
16
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Figure 1: Data Collection Design for Program Evaluation
75 villages
(3250 households)
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__________ _________________________________|__________________________________________
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|
|
|
|
15 villages
15 villages
15 villages
15 villages
15 villages
(650 households)
(650 households)
(650 households)
(650 households)
(650 households)
Randomized
Randomized
Randomized
Randomized
Randomized to
CCT to Father
CCT to Mother
UCT to Father
UCT to Mother
Control Group
|
|
|
|
|
|
|
|
|
|
 500 poor treated
 500 poor treated
 500 poor treated
 500 poor treated
 575 poor, nonhouseholds
households
households
households
treated
households
 75 poor non 75 poor non 75 poor non 75 poor nontreated
treated
treated
treated
 75 non-poor,
households
households
households
households
non-treated
households
 75 non-poor,
 75 non-poor,
 75 non-poor, non 75 non-poor,
non-treated
non-treated
treated
non-treated
households
households
households
households
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1. Anticipated Outputs and Dissemination Activities
During the project, as descriptive and analytical results accumulate, we will circulate policy
briefs to interested parties and post working papers. Dissemination through written materials and
frequent briefings and informal seminars in Ouagadougou will be ongoing throughout the
project. We will consider a variety of strategies to target the academic audience, the policy
makers and the national press.
Institutional Collaboration
This project is being coordinated with the following Burkina Faso government organizations,
international non-governmental organizations, and international agencies:
 University of Ouagadougou, Department of Economics
 Burkina Faso Ministry of Basic Education
 Burkina Faso Ministry of Secondary and Higher Education
 Burkina Faso Ministry of Social Action
2. Timeline
Social Protection Interventions and Household Survey Fieldwork
March-April 2008: Survey instrument pre-testing. Household census of 75 randomly selected
villages in Nahouri province and assignment of households to treatment and control groups.
May-June 2008: Pre-intervention baseline survey of 3250 households in 75 randomly selected
villages of Nahouri province.
June 2008-April 2009: Data entry and analysis of baseline survey
October 2008: Start of first year of intervention in treatment households
May-June 2009: First follow-up survey after one year of intervention
October 2009: Start of second year of intervention in treatment households
May-June 2010: Second follow-up survey after one year of intervention
3. Evaluation Team
The primary investigators of this project are Damien de Walque (DECRG), Harounan
Kazianga (Oklahoma State University), Richard Akresh (University of Illinois at Urbana
Champaign), and Mead Over (Center for Global Development). In addition, this team will be
supported by Yiriyibin Bambio, Jean-Pierre Savadogo and Pam Zahonogo from the University of
Ouagadougou in Burkina Faso. Akresh, de Walque, Kazianga and Over are responsible for the
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program design, and also responsible for the field work supervision. Bambio, Sawadogo and
Zahonogo will be responsible for the data collection. The intervention will be supervised by
Tshiya Subayi-Cuppen (AFTHD), the TTL of the Burkina health sector support and
multisectoral Aids program (HSSMAP) which will fund the intervention. The experimental
design has been approved by the governmental agency responsible for implementing the
interventions (Projet d’Appui au Programme Multisectoriel de Lutte contre le SIDA, PA-PMLS).
The CVs of the researchers are attached.
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Appendix 1: Summary of the survey instruments
A1.1 Household Survey
Household roster: Basic information on each household member including age, sex, relationship
to household head, literacy, main occupation and school attendance status.
Household assets: Sales, rental, purchases and gifts of land owned, livestock, farm equipment,
jewelry, durable goods (e.g. bicycles, radios, ploughs).
Production/Income module: Crop and livestock production and income from off-farm activities.
Consumption: Information on household consumption including own-consumption and
purchases of food and non-food items.
Health module: Information on individual health status, heath care seeking when sick, illness
burden on other household members (especially children committed to tend to sick adults).
Time use module: Individual time allocation, with focus on child time allocation between
attending school, studying, farm/livestock work, and household chores (in particular tending
younger siblings).
Transfers and credit: Intra and inter-household transfers made in-cash or in-kind; and intra and
inter-household lending and borrowing in-cash and in-kind.
Shocks and coping strategies: Major individual, household and community level negative and
positive shocks (death, illness, drought, theft) during the year and coping strategies.
Trust and risk preferences: Develop instruments to measure trust and risk preferences,
observational measure as well as limited lab experiments.
Anthropometric measures: Height and weight for all household children.
A1.2 Community level survey
Community Description: Basic information on the community including name, location
(possibly with GPS reference), year of creation, and administration level (commune, village etc).
Respondent characteristics: Basic information on the persons providing the information
Basic physical and demographic characteristics of the community: Information on community
size, population distribution by gender, religion, ethnicity, main occupation, access to arable land
and grazing.
Transportation/Access to cities and markets: Information on roads, distance to nearest cities,
access to market.
Public Interventions: Information on relevant public interventions in the communities, if any.
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Public finance: Source of funding of local public goods and other village level activities.
Management of these funds.
Political institutions: Traditional and modern political institutions (e.g. traditional chiefs, land
priests, elected village delegates, alderman).
Collective action: Measure the presence and the functioning of collective action entities (e.g.
youth and women associations, farmer cooperatives).
Weather/natural/health shocks: Information on rainfall (drought, flooding), harvest, pest attacks
and diseases (malaria incidence, meningitis).
A1.3. School level survey
Enrollment rate: In each village, for children between ages 6 to 15, by gender.
School staffing: Number of teachers, qualifications, and student/teacher ratios.
Teacher presence: Random check on teacher presence in each school, once per semester.
School infrastructure: Building structure, available seats, textbook availability.
Achievement tests: Scores on RAVEN and WISC tests administered by the survey team to all
children and success rates on national exam at the end of 6th grade.
A1.3. Health facility survey
General information on health facility: Identification and general description of health facility.
Characteristics of the health facility: Buildings, staffing, size of population served and type of
health services provided.
Human resources: Staff by gender, experience and by specialization, absenteeism.
Services, fees, and health utilization: Type of services offered and prices, and expressed demand
per unit of time.
Equipments: Lab and surgical equipment.
Health vignette: Use vignette to have a more objective measure of health care quality.
Exit interview: Randomly selected service users on waiting time, satisfaction level, and fees paid
including treatment, bribes, and transportation costs.
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