metadata: authors: 0: author: Evans,David
1: author: Holtemeyer,Brian
2: author: Kosec,Katrina L.
count: Tanzania
docna: 0: docna: Cash transfers and health : evidence from Tanzania
docty: Policy Research Working Paper
subtopic: Health Care Services Industry,Disability,Public Health Promotion,Health Economics & Finance,Educational Sciences,Services & Transfers to Poor,Health Insurance,Economic Assistance,Access of Poor to Social Services
abstracts: cdata!: How do conditional cash transfers impact
            health-related outcomes? This paper examines the 2010
            randomized introduction of a program in Tanzania and finds
            nuanced impacts. An initial surge in clinic visits after 1.5
            years -- due to more visits by those already complying with
            program health conditions and by non-compliers --
            disappeared after 2.5 years, largely due to compliers
            reducing above-minimal visits. The study finds significant
            increases in take-up of health insurance and the likelihood
            of seeking treatment when ill. Health improvements were
            concentrated among children ages 0-5 years rather than the
            elderly, and took time to materialize; the study finds no
            improvements after 1.5 years, but 0.76 fewer sick days per
            month after 2.5 years, suggesting the importance of looking
            beyond short-term impacts. Reductions in sick days were
            largest in villages with more baseline health workers per
            capita, consistent with improvements being sensitive to
            capacity constraints. These results are robust to
            adjustments for multiple hypothesis testing.
geo_reg_key: 517191
repnme: repnme: Cash transfers and health : evidence from Tanzania
display_title: Cash transfers and health : evidence
            from Tanzania
listing_relative_url: /research/2016/11/26917410/cash-transfers-health-evidence-tanzania
topicv3: Education m1327048 470,Cash Transfers m1327437 1608,Public Health m1327519 635,Health Insurance m1327759 1287,Health m1504661 3480
publishtoextweb_dt: 2016-11-07T00:00:00Z
no_of_pages: 52
author_keys: 0: author_key: 665679
model_extractions: WPS7882 Policy Research Working Paper 7882

# Cash Transfers and Health

## Evidence from Tanzania

_David K. Evans Brian Holtemeyer Katrina Kosec_ Africa Region Office of the Chief Economist November 2016
Policy Research Working Paper 7882

# **Abstract**

How do conditional cash transfers impact health-related outcomes? This paper examines the 2010 randomized introduction of a program in Tanzania and finds nuanced impacts. An initial surge in clinic visits after 1.5 years—due to more visits by those already complying with program health conditions and by non-compliers—disappeared after 2.5 years, largely due to compliers reducing above-minimal visits. The study finds significant increases in take-up of health insurance and the likelihood of seeking treatment when ill.

Health improvements were concentrated among children ages 0–5 years rather than the elderly, and took time to materialize; the study finds no improvements after 1.5 years, but 0.76 fewer sick days per month after 2.5 years, suggesting the importance of looking beyond short-term impacts. Reductions in sick days were largest in villages with more baseline health workers per capita, consistent with improvements being sensitive to capacity constraints. These results are robust to adjustments for multiple hypothesis testing.

This paper is a product of the Office of the Chief Economist, Africa Region. 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 at devans2@worldbank.org and k.kosec@cgiar.org.

_The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. 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 Health: Evidence from Tanzania David K. Evans Brian Holtemeyer Katrina Kosec<sup>_∗_</sup> The World Bank IFPRI IFPRI _JEL Classification:_ I18, I13, O12, H42 _Keywords_ : Cash transfers, health, government policy, health insurance

> _∗_ This study benefitted at various stages from experts at the World Bank, the International Food Policy Research Institute (IFPRI), the Tanzania Social Action Fund (TASAF) and elsewhere. At TASAF, the evaluation has been supported by the Executive Director Ladislaus Mwamanga, as well as the former Executive Director Servacius Likwelile. Amadeus Kamagenge has led TASAF input to the evaluation, and his entire team has contributed with substantive and logistical support. We are also grateful to Harold Alderman, Domenico Fanizza, Margaret Grosh, Melissa Hidrobo, Jef Leroy, David McKenzie, Berk Özler, Anna Popova, Dena Ringold, Shalini Roy, and Magnus Saxegaard for comments and helpful discussions. We received financial support from the CGIAR Research Program on Policies, Institutions, and Markets, the International Initiative for Impact Evaluation (3ie), the Strategic Impact Evaluation Fund (SIEF), and the Trust Fund for Environmentally and Socially Sustainable Development (TFESSD). Any comments or suggestions are welcome; the authors may be contacted at k.kosec@cgiar.org and devans2@worldbank.org.
# **1 Introduction**

What role can cash transfers conditioned on health-seeking behavior play in alleviating the burden of poor health and limited access to formal medical care in Sub-Saharan Africa? Meta analyses of programs from around the world suggest that conditional cash transfers (CCTs) can effectively alleviate extreme poverty and improve a range of human capital outcomes for children, at least during the period that the program is in place (Fiszbein and Schady, 2009; Leroy et al., 2009; Independent Evaluation Group, 2011). As the evidence base has grown, countries have raced to adopt CCTs. Almost every country in Latin America now has a CCT program (Fiszbein and Schady, 2009). Further, as of 2010, at least 14 countries in SubSaharan Africa had implemented a CCT program (Garcia and Moore, 2012). While there is considerable evidence about the impacts of cash transfers—conditional and unconditional— on education outcomes, less is known about their impacts on health. A 2014 global review found 142 studies showing the impact of cash transfers on education outcomes, but only 41 showing impacts on health and nutrition outcomes (Andrews et al., 2014).

Nowhere is the global burden of disease greater than in Sub-Saharan Africa. Life expectancy has increased by 20 years globally since 1970, but by only 10 years in SubSaharan Africa (Institute for Health Metrics and Evaluation, 2013; World Bank, 2013). Further, Africa has a lower growth elasticity of poverty than any other region (World Bank, 2013). The region’s health problems are partly due to a pervasive lack of health investment by the public and private sectors, resulting in limited access to doctors and health facilities.

Existing literature on the health impacts of cash transfers yields mixed results. There are several program types: unconditional cash transfers (UCTs) and CCTs conditioned on health, education, or both. Especially in Sub-Saharan Africa, conditions are often “soft” (e.g., warnings or small penalties are applied instead of withholding the full transfer), making the difference between CCTs and UCTs less stark (Garcia and Moore, 2012). Relatedly, Paxson and Schady (2010) find that 28 percent of those participating in a UCT program in Ecuador thought conditions applied. However, even among cash transfer programs of the 2
same type, there are often mixed impacts on health. Among UCTs, Haushofer and Shapiro (2016) find that a transfer program in Kenya improved mental health and increased food consumption. UCTs have been found to improve anthropometric outcomes for girls—though not boys—in South Africa (Duflo, 2003, 2000). However, Paxson and Schady (2010) find null overall impacts of a UCT in Ecuador on cognitive, behavioral, and physical outcomes for children, with only those in the bottom expenditure quartile benefiting. And Handa et al. (2015) find no overall impacts of a UCT in Zambia on maternal health care utilization, with positive impacts only for women with better access to health services. CCTs conditioned on health have improved early childhood cognitive development (Macours et al., 2012) and child nutritional status (Maluccio and Flores, 2005) in Nicaragua, improved child nutritional status for a select group of children (younger children from rural areas) in Colombia (Attanasio et al., 2005), and had null impacts in Brazil (Morris et al., 2004) and Honduras (Hoddinott, 2010).<sup>1</sup> Finally, several studies explicitly compare the impacts of UCTs versus CCTs. Akresh et al. (2014) find an increase in preventative health care visits for a CCT in Burkina Faso conditioned on education and health, but not for a comparison UCT arm. Robertson et al. (2013), in contrast, do not find systematic benefits of CCTs over UCTs in Zimbabwe. And Benhassine et al. (2015) find that adding formal conditions to a labeled cash transfer (LCT) in Morocco—not subject to education conditions, but explicitly labeled as an education support program—may have _decreased_ the overall impact of the program on school participation and learning. Similarly, for a CCT in Malawi conditioned on education, Baird et al. (2011) find that the UCT arm saw a greater reduction in teenage pregnancy among girls who had dropped out of school than did the CCT arm. And in the same study context, Baird et al. (2013) find greater mental health improvements and increases in usage of shoes among girls enrolled in school in the UCT arm than in the CCT arm. Given inconclusive findings in the literature on the health benefits of cash transfers, even among

> 1A few studies examine more specialized CCTs. Interventions in India and Nepal offered incentives for maternal health investments, with mixed results (Powell-Jackson et al., 2015; Powell-Jackson and Hanson, 2012). And interventions in Tanzania and Lesotho have provided incentives to remain free of sexually transmitted diseases, with positive outcomes (Bjorkman Nyqvist et al., 2015; De Walque et al., 2014).

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programs with similar designs, there is a need for greater understanding of the mechanisms through which cash transfers impact health.

We examine the impacts of a 2010 pilot CCT program in rural Tanzania on a range of health investments and outcomes. Among 80 study villages, 40 were randomly assigned to receive the CCT program, allowing us to estimate its causal impacts. Beneficiaries included both children aged 0–15 and elderly individuals aged 60 and older. Conditions of the program included visits to health clinics by young children aged 0–5 and by the elderly. Households were surveyed at baseline in 2009, again in 2011 after 18-21 months (about 1.5 years) of transfers, and finally in 2012 after 31-34 months (about 2.5 years) of transfers.

We find nuanced impacts of the CCT program. An initial surge in clinic visits after 1.5 years—due to more visits by both those already complying with program health conditions and non-compliers—disappeared after 2.5 years, largely due to compliers reducing aboveminimal visits. We also find significant increases in take-up of health insurance. After 2.5 years, the program made households in treatment villages 36 percentage points more likely to participate in the government-run health insurance program (the Community Health Fund, or CHF) and raised the likelihood of financing treatment with health insurance by 16 percentage points. These impacts on health insurance are particularly interesting. Little previous work has examined the impact of cash transfers on participation in health insurance programs. Evidence from Mexico suggests that participation in a CCT program increased participants’ awareness that they were enrolled in a health insurance program, but in that case, actual enrollment was automatic upon enrollment in the cash transfer program (Biosca and Brown, 2014). The CCT additionally increased the likelihood of seeking treatment when ill. This latter result is important given recent research showing that timely clinic attendance when ill improves child health outcomes in Tanzania (Adhvaryu and Nyshadham, 2015). We also find that the program led to significantly higher investments in preventative health measures, including an 18 percentage points increase in shoe ownership, which the public health community associates with lower exposure to helminths (Mascarini-Serra et al., 4
2011; Birn and Solórzano, 1999). Health improvements were concentrated among young children aged 0–5, with no detectable health improvements for elderly individuals similarly required to visit health clinics. Further, health improvements took time to materialize; we observe no improvements after 1.5 years, but 0.76 fewer sick days per month for 0–5 year olds after 2.5 years.<sup>2</sup> This suggests the importance of looking beyond very short-term impacts. Reductions in sick days were largest in villages with more baseline health workers per capita, consistent with improvements being sensitive to capacity constraints.

Overall, this evidence suggests a variety of mechanisms through which cash transfers may help to lift the burden of disease in Sub-Saharan Africa. We further show that these results are robust to adjustments for multiple hypothesis testing, estimation of linear as well as non-linear models, and both intent-to-treat and treatment on the treated estimates.

The remainder of the paper is organized as follows: Section 2 provides background information on health and the health care system in Tanzania, as well as the health conditions of Tanzania’s pilot CCT program. Section 3 describes the evaluation design, data, and outcomes of interest. Section 4 presents our empirical specification, the groups over which we examine heterogeneous treatment effects, balance tables showing the outcome of our randomization, and analysis of attrition. Section 5 characterizes our main empirical results and several robustness checks. Section 6 considers how our main impacts vary across different types of villages and households, and what this implies for the mechanisms likely driving treatment effects. Section 7 concludes.

# **2 Background**

## **2.1 Health care and health in rural Tanzania**

Tanzania is, in many respects, close to the Africa regional average in terms of health statistics. In 2012, 17.3 percent of the population contracted malaria versus 18.6 percent in Africa as a

> 2When we refer to illness in the last month, we are in all cases referring to the last four weeks.

5
whole. Likewise, 3.1 percent of the population was HIV positive, versus 2.8 percent in Africa. Life expectancy at birth is 61 years versus 58 for Africa. Yet on some measures, Tanzania diverges significantly from the rest of the region. Its under-five mortality rate (5.4 percent of live births) is just over half that of Africa as a whole (9.5 percent). Its maternal mortality ratio is almost 20 percent lower than that of Africa. Yet the health workforce is weaker in Tanzania, with just 0.1 doctors and 2.4 nurses and midwives per 10,000 population (versus an average of 2.6 and 12.0, respectively, for Africa) (World Health Organization, 2014).

Recent evidence from Tanzania demonstrates significant health improvements for children utilizing formal public health facilities (Adhvaryu and Nyshadham, 2015). In the early 1990s, the Tanzanian government introduced a health insurance program called the Community Health Fund (CHF). It is a voluntary prepayment scheme; members pay a fixed annual fee – – of 5,000 10,000 Tanzanian shillings ($3 $6 US),<sup>3</sup> depending on the region. Their entire family is then exempt from co-payments for visits to primary health care facilities (Marriott, 2011).<sup>4</sup> As Tanzania’s CHF cross-subsidizes more costly to reach rural areas, it provides not only a risk-coping strategy, but also significantly reduces total out-of-pocket health expenses by the poorest (such as CCT program beneficiaries in our study regions) (Ekman, 2004; Mtei et al., 2007). This is especially so since the poorest are often credit constrained. Nonetheless, 10 years after the introduction of the CHF, only 10 percent of Tanzanians were enrolled; one of the reasons cited was inability to pay (Kamuzora and Gilson, 2007).

# **2.2 Pilot CCT program**

Tanzania’s pilot CCT program, implemented by the Tanzania Social Action Fund (TASAF, a social fund agency of the Tanzanian government), began delivering transfers in January of 2010. Its aims were to increase investments in health for young children (ages 0–5) and the elderly (ages 60 and over) and to increase educational investments for children aged 7–15. It

> 3In 2009 the exchange rate ranged from 1,280 to 1,467 per U.S. dollar (Bank of Tanzania, 2015).

> 4Up to 7 family members are exempt from co-payments—though tests and medications are subject to fees. Upon introduction of the CHF, child and maternal health services were already exempt from co-payments according to official government policy (Babbel, 2012).

6
operated in three districts—Bagamoyo (70 km from Dar es Salaam), Chamwino (500 km), and Kibaha (35 km)—where 80 eligible study villages were randomized into treatment and control groups of 40 villages each, stratified on village size and district (median village size at baseline was 560 households). Randomization was carried out after identification of potential beneficiary households in all 80 villages. At village meetings held prior to randomization, TASAF communicated that control villages would receive the program in late 2012, and the program would continue in treatment villages. Median village size was quite small (560 households at baseline, in 2009), and every village had both a primary school and a public dispensary or health center, facilitating fulfillment of program conditions.

Treatment households received transfers every two months. Transfer amounts ranged from US $12 to US $36, depending on household size and composition. The CCT provided US $3 per month for orphans and vulnerable children up to age 15 (approximately 50 percent of the food poverty line) and US $6 per month for vulnerable individuals age 60 or older. In our follow-up surveys, the median size of the last transfer is US $14.12; assuming six annual payments of this size, this is about 13 percent of annual household expenditures.

While CCT payments were made at the household level, conditions applied at the individual level.<sup>5</sup> Children aged 0–5 had to visit a health clinic at least six times per year (the condition was relaxed for children aged 2–5 to two visits per year starting in 2012),<sup>6</sup> those age 60 or over had to visit at least once per year, and no health conditions applied to others. Both preventive and curative visits fulfilled the health clinic visit conditions of the program, though visits had to be to a public facility (either a dispensary, health center, or hospital). There were no further restrictions on the timing of visits, nor on the services to be received. Children aged 7–15 had to enroll in school and maintain an 80 percent attendance record.

> 5We lack administrative data on compliance with conditions. However, in each follow-up survey, we asked: “[For your last transfer payment,] did you receive less money than you usually get?” and “What do you think was the reason?” While one may hesitate to admit to non-compliance (for fear of sanction) and while this cannot tell us how many households had at least one payment reduced (it only tells us about the last), this gives some indication of compliance levels. At midline and endline respectively, 1.9 and 3.0 percent of treatment households reported receiving less than usual for a reason related to not meeting conditions.

> 6As our endline survey was carried out during August–October 2012, we define compliance with clinic visit conditions at endline for 2–5 year olds as having two or more clinic visits in the last year.

7
TASAF worked with an elected community management committee (CMC) in each village to select beneficiary households.<sup>7</sup> The CMC surveyed the poorest half of households, collecting data on eight household characteristics: roof material, light supply, water supply, type of toilet, ownership of four different assets (vehicle/motorcycle, radio, iron, poultry), number of windows on the house, household size, and number of meals eaten per day. TASAF then carried out a proxy means test to propose a ranking of households by poverty level, for CMC and village leader approval. On average, 23 percent of households became beneficiaries.

# **3 Evaluation Design and Data**

## **3.1 Evaluation design**

We evaluate the impacts of the CCT program using three waves of data on beneficiaries and would-be beneficiaries (no data were collected from those not selected to be beneficiaries). Table 1 presents the chronology of the program and impact evaluation. A baseline survey was carried out during January–May 2009 and payments began in January 2010. A midline survey was conducted during July–September 2011 (18-21 months after transfers began) and an endline survey was conducted during August–October 2012 (31–34 months after transfers began). The baseline survey included 1,764 households (a subset of beneficiary households) comprised of 6,918 individuals. The quantitative data collection was supplemented by two rounds of qualitative data collection (following the midline and endline surveys) employing focus group discussions and in-depth interviews.

## **3.2 Data and outcomes**

In each of the three survey rounds, we collected individual-level data on total health clinic visits in the last year,<sup>8</sup> ownership of protective footwear (shoes and slippers) by children,

> 7CMC elections occurred at village meetings; 10–14 members were elected, with secret ballots. To run, a candidate had to have received financial training and successfully managed a past TASAF-supported project.

> 8We lack data on whether such visits were for preventive or curative purposes, and only know the total.

8
health (whether an individual was ill in the last month, and for how many days in the last month they were unable to perform their normal daily activities due to illness), reported ability to perform ordinary activities (doing vigorous activity, walking uphill, bending over or stooping, walking more than 1 km, walking more than 100 meters, or using a bath or toilet), anthropometrics (height, weight, middle upper-arm circumference, and z-scores for height-for-age, weight-for-age, weight-for-height, and body mass index-for-age), and—for those ill in the last month—the location where medical care was sought (no treatment sought, public dispensary, public hospital, public health center, private pharmacy, traditional healer, private dispensary/ hospital/ clinic, or mission dispensary/ hospital).<sup>9</sup> Among those seeking treatment, we further gathered data on health care financing methods (free treatment, loans, cash or assets, or health insurance). We also collected household-level data on expenditure on formal insurance<sup>10</sup> and—at endline—whether the household participates in the CHF.

# **4 Methods and Empirical Strategy**

## **4.1 Empirical specification**

We carried out follow-up surveys in 2011 and in 2012 to capture both short-term (1.5 years) and medium-term (2.5 years) impacts of the program. Given random assignment to treatment, we recover causal intent-to-treat estimates from the following empirical specification: where _i_ indexes individuals and _t_ indexes the survey round. _hit_ is a health-related outcome, _αi_ are individual fixed effects, _Ti_ =1 in a village assigned to treatment and zero otherwise, 2011 _t_ =1 at the time of the midline survey (July–September 2011) and zero otherwise, and

> 9Data on protective footwear were only collected for children aged 0–18, data on anthropometrics for children aged 0–5, and data on ordinary activities for those aged 60 and over. Individuals sick in the last month were asked to report the primary health provider and payment method for their main health problem.

> 10Insurance expenditure data are unfortunately not further disaggregated by type of insurance.

9
2012 _t_ =1 at the time of the endline (August–October 2012) and zero otherwise. When we consider a household-level outcome, _i_ instead indexes households.

In treatment villages, 9.0% of households did not receive treatment—likely due to lastminute changes in community prioritization or household refusal. In control villages, 0.6% of households received treatment—likely due to their proximity to a treatment village. As a result, our intent-to-treat estimates represent a lower bound on the actual impact of receiving transfers. We also estimate the effect of treatment on the treated by using the fitted values from a regression of treatment on assignment to treatment in place of _Ti_ in equation 1.<sup>11</sup>

# **4.2 Heterogeneous treatment effects examined**

We estimate the overall impacts of the CCT program as well as its impacts on several subgroups. First, we examine impacts by age group. As health conditions applied only to children aged 0–5 and elderly aged 60 and over, and given that each of these two age groups has a different set of health issues and faced different conditions under the CCT program, it is instructive to examine program impacts on them separately. Overall impacts include all individuals in the surveyed households, not only all individuals in the two sub-groups.

Second, for two central outcomes likely to be heavily influenced by the quality of available health care—health clinic visits and health during the last month—we examine heterogeneous impacts of the CCT program by baseline health clinic staff (doctors, nurses, and other assistants) per capita. Specifically, we divide villages into two types: those with abovemedian and below-median health clinic staff per capita at baseline. This helps us assess if improvements are sensitive to capacity constraints Finally, for outcomes likely to be influenced by how credit constrained a household is— shoes and slipper ownership, expenditure on insurance, participation in the CHF, whether one treats illness and where (public or private facilities), and how one finances treatment— we examine heterogeneous impacts by baseline household asset wealth. This allows us to

> 11 We use the Stata package –xtivreg– written by Schaffer (2010).

10
observe how the program affects the moderately poor (top half of beneficiaries in terms of asset wealth) versus the extremely poor (bottom half). To capture asset wealth, we carry out a principal components analysis (PCA) using dummy variables for ownership of 13 assets.<sup>12</sup>

# **4.3 Outcome of the randomization**

A comparison of baseline sample means in treatment and control villages reveals balance on most outcomes (Appendix Table A1, Panel A). Across 41 outcomes, for only six (three) are there significant differences at the 10 percent (5 percent) level. There are no overall differences in health between treatment and control villages, but 0–5 year olds in treatment villages were 6 percentage points more likely to be ill or injured and had 0.51 more sick days in the last month than those in control villages. Weight-for-age z-scores were slightly lower in treatment villages. And 0–18 year olds in treatment villages were 10 percentage points less likely to own shoes than were those in control villages. Households in treatment villages also spent slightly more on insurance. However, we see balance on all other outcomes of interest. Table A1, Panel B shows similar balance on individual and household demographic characteristics and village characteristics. The only significant difference is that treatment households are less likely to have an improved floor. We use individual (or household, for outcomes that vary at that level) fixed effects to account for baseline imbalances.<sup>13</sup>

# **4.4 Attrition**

If attrition were correlated with treatment status, one might worry that attrition had compromised the internal validity of the results.<sup>14</sup> Fortunately, this is not the case, as shown in Table A2. Columns (1)–(4) consider household attrition, columns (5)–(8) consider individual

> 12These include whether the household owns an iron, refrigerator, television, mattress or bed, radio, watch or clock, sewing machine, stove, bicycle, motorcycle, car or truck, wheelbarrow or cart, and mobile phone. 13 In the case of anthropometric outcomes, we use village _×_ cohort fixed effects. These results are robust to instead using individual fixed effects.

> 14Between baseline and midline, 8.6 percent of households attrited from the sample, and between baseline and endline, 13.2 percent of households attrited.

11
attrition, and columns (9)–(12) consider individual attrition for those for whom health conditions applied (children aged 0–5 and those aged 60 and over). For each of the three analyses, we consider attrition at midline and at endline. Odd-numbered columns regress a dummy for attrition on our treatment dummy, while even-numbered columns regress a dummy for attrition on our treatment dummy, an array of controls (gender, age, age-squared, a dummy for having some education, and a household asset index), and the interactions of these controls with treatment. Where we examine household attrition, we use the values of these controls for the household head; where we examine individual attrition, we use the values for the head as well as the individual. In no case does the treatment dummy significantly predict attrition. F-statistics for the joint significance of the treatment dummy and the interaction terms further indicate that these coefficients are never jointly significant. Overall, we conclude that attrition does not affect the internal validity of our results.

# **5 Results**

## **5.1 Health clinic visits**

At baseline, the average 0–5 year old visited a clinic 8.3 times per year (compared to the program condition of six visits), and the average individual aged 60 or older visited 2.8 times (compared to the program condition of one visit). This reveals that on average, individuals were exceeding program conditions at baseline.<sup>15</sup> Universal compliance with the program could thus occur at follow-up even with a zero net increase in clinic visits if more frequent visits by those not previously in compliance were offset by less frequent visits by those already complying at baseline. In Table 2, we examine the impact of the CCT program on the number of health clinic visits in the last year. We focus on overall impacts, impacts on children aged 0–5, and impacts on those age 60 and over. (At endline, we have clinic visit

> 15At baseline, 59 percent of children aged 0–5 and 65 percent of those aged 60 and over met or exceeded required health clinic visits, making program conditions non-binding for them.

12
data for all individuals, while at midline, we only have it for these two groups.) At midline (1.5 years after treatment began), treatment led to 2.3 more visits (preventive or curative) per year for children aged 0–5 (column 2) and 1.1 more visits for those aged 60 and over (column 3). Relative to the baseline mean number of visits for each age group, these represent increases of 28 and 39 percent, respectively, which are comparable to findings in the literature. For example, Levy and Ohls (2007) find that a CCT program in Jamaica increased preventive health center visits by children aged 0–6 by 0.28 visits every six months (a 38 percent increase relative to the baseline mean), while Akresh et al. (2014) find that a CCT program in Burkina Faso increased annual preventive care visits by children aged 0–5 by 0.43 visits (a 49 percent increase relative to the control group mean). These statistically significant effects, however, disappear at endline (2.5 years after treatment began) for both age groups.<sup>16</sup> The results are robust to instead estimating a Poisson model that accounts for health clinic visits being a count data outcome (Appendix Table A9)<sup>17</sup> and to instead estimating the impact of treatment on the treated (Appendix Table A3).

In Table 3, we examine the impact of the CCT program on the rate of compliance with annual clinic visits conditions. While we lack administrative data on clinic visits, comparing self-reported visits over the last 12 months with program conditions for total annual visits is instructive. The conditions required six visits for those under age 2 and one visit for those over age 60; 2–5 year olds needed six visits at midline but two visits at endline. We see that treatment increased compliance with program conditions among both 0–5 year olds and those over aged 60 at midline. By endline, however, treatment increase compliance with program conditions only among those over aged 60, and not among children aged 0–5.

Several caveats and observations are warranted. First, households in control villages that by endline anticipated receiving the program within a few months<sup>18</sup> may have increased

> 16At endline, those in treatment villages were still receiving the CCT program and expected it to continue. Those in control villages anticipated being enrolled within the next few months (by late 2012).

> 17Results hold whether we use heteroskedasticity robust or bootstrapped standard errors.

> 18The endline survey was carried out during August–October 2012, and control villages were told at baseline to anticipate receiving the program in late 2012.

13
clinic visits preemptively for fear of being cut from the list of targeted households. Indeed, when we consider compliance with clinic visit as our outcome (Table 3), we find a positive and highly statistically significant coefficient on the endline dummy for 0–5 year olds— consistent with an overall increase in childrens’ compliance with program conditions across both treatment and control villages at endline. Second, it is important to interpret these findings in light of high baseline rates of compliance that made the health visit conditions non-binding for many.<sup>19</sup> Program emphasis on clinic visits may have increased the salience of health services and led households to initially increase visits despite the average household already satisfying visit conditions. Subsequently—by endline—individuals’ understanding of the conditions may have improved, and they may have reduced visits to only those that were necessary, still exceeding the program conditions on average. Third, health improvements due to the program that were realized by endline but not at midline—detailed in Section 5.4—may have reduced demand for clinic visits by endline. Finally, while we lack data on clinic service quality, it may have improved by endline, requiring fewer visits to receive similar care (e.g., receiving more and better services at a first visit could preclude the need for a follow-up visit). We present further evidence and discussion of why clinic visits may have increased at midline, but were subsequently unaffected at endline, in Section 6.

# **5.2 Protective footwear**

While health clinic visits are an important aspect of individual investment in health, investments that individuals make to prevent health problems from occurring are also important. We examine the impacts of treatment on ownership of two types of protective footwear: shoes and "slippers" (i.e., open-toed footwear). Table 4 shows that the CCT program led to a significant, 18 percentage point increase in shoe ownership among 0–18 year old children by midline that persisted at endline (column 1).<sup>20</sup> A null impact on slipper ownership at midline

> 19While non-binding conditions make a CCT similar to a UCT or LCT, Section 1 discusses how UCTs are prevalent, and many CCTs have soft conditions. Thus, our study context is not atypical.

> 20Estimates of the effect of treatment on the treated are similar (Appendix Table A4).

14
changed to a significant, 8 percentage point increase by endline (column 2). This suggests that the program did not lead to a substitution between shoes and slippers, but rather increased take-up of both products by endline. Further, impacts were largest for ownership of shoes—which provide better protection. These impacts are remarkable considering baseline ownership rates of shoes and slippers were only 42 percent and 63 percent, respectively.

# **5.3 Health insurance**

We also examined program impacts on take-up of health insurance. As we discuss in Section 2, participation in Tanzania’s government-run health insurance program, the CHF, should not only help households cope with the risk of health shocks, but also reduce out-of-pocket expenditures on health given cross-subsidies built into the scheme, favoring the rural poor. Table 4 shows that treatment increased household expenditures on insurance sixfold by midline and eightfold by endline (column 3). It also increased participation in the CHF; while we lack baseline data on participation rates, by endline, households in treatment villages were 36 percentage points more likely to participate than were households in control villages (column 4). This is strikingly large given that at baseline, only 3 percent of individuals who sought treatment for illness in the last month reported using health insurance to fund it.

Table 5 examines the health care financing methods of individuals who reported being ill in the last month and treated the illness.<sup>21</sup> We find that at midline, the program reduced payment for health care using cash or an asset by 18 percentage points, which is a 27 percent decrease from the baseline mean of 65 percent. This same effect size was sustained at endline. Those no longer financing treatment with cash and assets began using health insurance; we see a 16 percentage point increase in use of health insurance at midline to finance treatment, which swelled to 28 percentage points by endline (from a baseline mean of only 2.7 percent).

> 21In Appendix Table A5, we examine whether treatment affects selection into who reports being ill or injured in the last month. We find that few interactions of individual and household characteristics with treatment are statistically significant predictors of illness or injury. Further, when we conduct a test of the joint significance of these interaction terms for individuals for whom health conditions applied (those aged 0–5 and aged 60 and over), we find insignificance at both midline (p = 0.369) and endline (p = 0.612).

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Our findings on health insurance may be driven by several factors. First, if liquidity has been a binding constraint, a CCT program may increase take-up of insurance.<sup>22</sup> Second, the CCT program may have improved access to information about the CHF and lowered barriers to enrollment. In qualitative data, health clinic staff in treatment villages reported going to the place where beneficiaries collected transfers to tell them about the CHF and encourage sign-up while they still felt rich (Evans et al., 2014). Finally, other research on the same CCT finds that it increased familiarity with and trust in local leaders and health care providers (Evans et al., 2016). Combined with evidence that trust increases take-up of insurance (Dercon et al., 2015), this too may explain increased participation in the CHF.

# **5.4 Health**

Table 6 reports the effects of treatment on two key health outcomes: whether or not an individual was ill or injured in the last month, and the number of days that the individual was unable to perform their normal daily activities in the last month due to illness (sick days) (Panel A). These capture, respectively, the extensive and intensive margins of illness. We see that at midline, treatment had no significant impact on either health outcome. However, at endline, treatment significantly reduced both the extensive and intensive margins of illness. In particular, for the sample as a whole, treatment resulted in a 4.3 percentage point reduction in the incidence of illness or injury in the last month (p-value = 0.101); while of borderline statistical significance, this is a sizeable 17 percent decrease relative to the baseline mean incidence of 27.6 percent. When we instead compute the effect of treatment on the treated (Appendix Table A6), we observe a statistically significant (p < 0.10), 4.6 percentage point reduction in incidence of illness or injury in the last month. For the sample as a whole, treatment also resulted in a statistically significant, nearly half-day decrease in sick days in the last month (a 27 percent decrease relative to the baseline mean of 1.64 sick

> 22A desire to insure against health shocks can be understood in light of the frequency of such shocks in our study context; at baseline, 55 percent of households reported experiencing a health shock in the last five years (specifically, a chronic or severe illness or accident of a household member, or a death in the family).

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days). These treatment effects seem to be strongly driven by health improvements for young children (ages 0–5), for whom the reduction in incidence of illness in the last month is 10.7 percentage points (significant at the 10 percent level) and the reduction in sick days is 0.76 (significant at the 5 percent level). We find no significant overall program impacts for those aged 60 and over, either on the extensive or the intensive margins.<sup>23</sup> Similar results hold when we instead estimate a Poisson model (Appendix Table A9). While the program has health benefits, these take time to materialize, are most prominently on the intensive rather than extensive margin of illness, and accrue predominately to young children.

Despite overall health improvements, the CCT program did not change the ordinary activities that elderly individuals could perform, as shown in Appendix Table A10. Specifically, it did not have significant impacts on individuals’ reported ability to do vigorous activities, walk uphill, bend over or stoop, walk more than 1 km, or use a bath or toilet, nor did it affect a simple 0–6 index of these activities (the “ordinary activities index”). One exception is the ability to walk more than 100 meters (a dummy that had a very high baseline mean of 0.96); there, we find a very small negative impact of the program at endline. Overall, however, the program did not have systematic impacts on the types of activities that individuals could perform; rather, it changed the number of days that they could perform their activities.

There are several reasons that health may have improved. First, given that the CCT program increased health clinic visits at midline, this increased health-seeking behavior may have itself improved health by endline. Second, additional income, insurance, and the added familiarity with health clinics generated by the program may have spurred individuals to visit clinics promptly whenever ill, thus reducing the duration of illness. We explore this possibility in Section 5.6; if clinic visits were better timed (even if their aggregate numbers did not increase), this might explain why our results on the intensive margin of illness are the most robust. Third, the program may have generally stimulated health-promoting investments by households. Existing research on the CCT program shows that it did not

> 23Treatment did not affect rates of mortality or the number of household members in different age groups (Appendix Tables A7, A8, and Panel C of Appendix Table A9).

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increase food consumption during the last week at either midline or endline, but that it did increase expenditures on non-food items in the last 12 months—including on women’s and children’s clothing—and increased the number of goats and chickens households owned (Evans et al., 2014). Further, the program increased children’s shoe ownership (Section 5.2). The findings on improved health demonstrate the importance of taking care to evaluate health outcomes after an appropriate period of time, as advocated in general by King and Behrman (2009). At least in this study, positive health impacts do not appear after 1.5 years of transfers, though do appear after 2.5 years. In Section 6, we present further evidence and discussion on why health may have improved by endline but not midline, and what role program health conditions may have played in delivering health benefits.

# **5.5 Anthropometrics**

Appendix Table A11 reports the effects of treatment on a number of anthropometric outcomes for children aged 0–5: height-for-age, weight-for-age, weight-for-height, body mass index (BMI)-for-age, height, weight, and middle upper-arm circumference (MUAC) (columns 1–7, respectively). These regressions use village _×_ 6-month age cohort fixed effects since very few children were in the 0–5 age range for multiple observations during 2009–2012. We find no evidence that treatment influences these outcomes.<sup>24</sup> The lack of anthropometric effects is striking; it contributes to a mixed literature on the impacts of CCTs on child anthropometrics (Fiszbein and Schady, 2009). The result is less surprising when considering the null impacts of the program on food consumption (Evans et al., 2014).

# **5.6 Health care provider type**

Table 7 examines the impacts of the CCT program on health care provider decisions of individuals who reported being ill in the last month.<sup>25</sup> Individuals either fail to treat their

> 24We also find null results when only considering children under age 2.

> 25At baseline, 28 percent of individuals reported being ill or injured in the last month; 85 percent sought treatment for their illness—49 percent in the public sector and 36 percent in the private sector.

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main health problem (15 percent did so at baseline) or visit one of several different types of public and private providers. As the health conditions of the program required visits to be at public facilities, we anticipated finding larger impacts of treatment on public than on private facility visits. We find that at midline, the program reduced failure to seek treatment by 12 percentage points (column 1). That illness was more likely to be treated may explain why health impacts were most robust on the intensive margin, with the CCT program generally contributing to shorter spells of illness. At both midline and endline, the program increased use of public dispensaries; by 17 percentage points at midline, and 15 percentage points at endline (column 2). However, it did not impact use of private providers (columns 5–8). This is consistent with the health clinic visit conditions of the program, which counted only visits to public facilities and not private facilities. Rather than drawing individuals from the private to the public sector, we see a shift from a failure to treat illness to treatment at a public dispensary. Further, the program did not lead individuals to treat illness at a public hospital or a health center (columns 3–4). These are larger facilities that would typically offer more services (and potentially more qualified staff), but which are usually further away.

# **5.7 Robustness: Corrections for multiple hypothesis testing**

A growing literature recognizes the risk of finding false positives when testing multiple hypotheses and advances correction methods. Two popular methods are the Benjamini and Hochberg (BH) and the Benjamini–Krieger–Yekutieli (BKY) methods, which control for the false discovery rate (FDR) (Benjamini and Hochberg, 1995; Benjamini et al., 2006). We compute the q-values (i.e., p-values corrected for multiple testing) of each. As a third test, we apply a Bonferroni correction—a method of controlling the family-wise error rate (FWER) that involves multiplying each p-value by the number of tests performed. While simple to compute, it suffers from poor power (Anderson, 2008) and is often used as an upper bound on the FWER (Hochberg, 1988). We thus rely primarily on the BH and BKY results, but take the Bonferroni as a useful guide to the lower bound of the significance of our results.

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Appendix Table A12 reports the resulting q-values from the three correction methods for all originally statistically significant impacts. For each method, a group of hypotheses is defined by the follow-up survey round (midline or endline) and broad type of outcome being considered (e.g., child anthropometrics or ordinary activities). This is usually equivalent to grouping together all of the hypotheses within a table for a given survey round.<sup>26</sup> Hypotheses associated with heterogeneous treatment effects are grouped with the hypotheses of overall treatment effects, despite being displayed in separate tables. In total, we observe 61 statistically significant impacts of the CCT program in the paper’s main tables. When we correct for multiple testing using the BKY (BH) method, 45 (43) remain significant. With the more conservative Bonferroni method, 35 remain significant.

Our main conclusions still hold. Under all three correction methods, the program significantly increased health clinic visits at midline but not endline. Furthermore, it boosted children’s shoe ownership and household expenditure on insurance at both midline and endline. Reductions in the intensive margin of illness by endline are still significant with both BKY and BH, though reductions in the extensive margin of illness do not survive these corrections. This may indicate that the CCT program’s ability to reduce illness is principally concentrated in its reduction of the severity of illness—and how debilitating it becomes— rather its incidence. Notably, under all three corrections, our finding that the program increases participation in the CHF remains statistically significant at the 1 percent level. Similarly, findings that the CCT program reduced the likelihood of failing to treat illness at midline, and increased visits to public dispensaries (but not private ones) at both midline and endline remain robustly significant under all three corrections. Finally, at both midline and endline, the finding that the program reduced use of cash or assets to finance health care and boosted usage of health insurance are again significant under all three corrections.

> 26There are three exceptions. In Table 4, protective footwear outcomes are grouped separately from insurance-related outcomes—just as they are separately considered in Section 5. In Table 6, hypotheses related to the extension and intensive margins of health are grouped separately. And in Appendix Table A10, we omit the ordinary activities index from our grouping; estimation of impacts of treatment on an index simply serves as an additional check on the robustness of these null findings.

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# **6 Mechanisms**

We gain additional insight into the mechanisms likely driving the impacts of treatment by separately examining sub-groups of beneficiaries. We already considered impacts by age group. However, as we discuss in Section 4.2, we also consider two additional types of heterogeneous treatment effects. For two central outcomes likely to be heavily influenced by the quality of available health care—health clinic visits and health during the last month—we examine heterogeneous impacts on villages with above-median versus below-median health clinic staff per capita at baseline. This helps us assess if improvements are sensitive to capacity constraints. For outcomes likely to be influenced by how credit constrained a household is—shoes and slipper ownership, expenditure on insurance, participation in the CHF, whether one treats illness and where (public or private facilities), and how one finances treatment—we examine heterogeneous impacts in moderately poor households (top half of beneficiaries in terms of asset wealth) versus extremely poor households (bottom half).

## **6.1 Impacts by health clinic staffing levels**

When we examine heterogeneous treatment effects by baseline health clinic staff per capita (Table 8), several interesting findings emerge. First, Panel A reveals that we cannot reject the null hypothesis that the CCT program had the same effect on health clinic visits in villages with few baseline health staff per capita (the bottom half of the distribution) as in villages with many (the top half). This is true overall and for both age groups (0–5 year olds and those age 60+). This provides suggestive evidence that the impacts of treatment on clinic visits would not be enhanced by increasing clinic staff per capita. Second, Panel B shows heterogeneous impacts on health by baseline clinic staff per capita. Here, we find that reductions in sick days are concentrated in villages with more health staff per capita, with no significant impacts in villages with few staff per capita. For individuals in villages that were highly-staffed at baseline, the average reduction in sick days in the last month is 21
0.96 (compared to an insignificant 0.07 days in more poorly-staffed villages). The difference between these two effects is statistically significant at the 5 percent level. This suggests that reductions in the intensive margin of illness may in fact be conditional on a village having sufficient staff to attend patients and treat illness. It is important to note, however, there there are no differential impacts of the program by baseline staffing levels on sick days for children aged 0–5. Clinic staffing may matter more for older individuals—possibly as they are less integrated into the health system. Additionally, there are no differential impacts of treatment on the incidence (extensive margin) of illness by clinic staffing levels.

Appendix Figure A1 helps illustrate these impacts. Sub-figure (a) presents two villagelevel scatterplots—one for midline, one for endline—each with 80 data points: 40 show treatment village averages (in black circles), and 40 show control village averages (in gray squares). We plot on the y-axis the average change in the number of sick days in the last month between baseline and follow-up (positive numbers indicate an increase, negative a decrease) and on the x-axis village health clinic staff per capita at baseline. We include separate linear fits for treatment and control. At midline, we see that there are essentially no health improvements in either treatment or control villages, across the full distribution of clinic staff per capita. By endline, however, treatment villages on average have greater reductions in sick days than do control villages across the full range of values of staff per capita. However, the difference is greatest in villages with especially high staff per capita.

Sub-figure (b) of Appendix Figure A1 presents a similar analysis where the outcome is now the average change in the number of clinic visits in the last year between baseline and follow-up. At midline, treatment villages on average experience larger increases in clinic visits than do control villages across the full range of values of clinic staff per capita. While the difference is greater in villages with higher staff per capita, this difference was not statistically significant in regressions. At endline, we see similar reductions in clinic visits in treatment and control villages across the full distribution of staff per capita—possibly reflecting better average health at endline (as seen in sub-figure (a)) that alleviated capacity constraints.

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# **6.2 Impacts by household wealth**

Examining heterogeneous treatment effects by baseline household asset wealth (Table 9) reveals several interesting results. First, as shown in Panel A, we do not find significant differences in the impacts of the program on whether one treats illness (column 1), and whether or not they treat it in a public dispensary (column 2), according to baseline household wealth.<sup>27</sup> However, Panel B shows that the impacts of the CCT program on shoe ownership (column 1), slipper ownership (column 2), and insurance expenditures (column 3) are responsive to baseline household wealth. For each of the three, the impacts of treatment are larger for the extremely poor (those in the bottom half of asset wealth at baseline) than for the moderately poor for both follow-up survey rounds. These differences are in several cases statistically significant. At midline, the extremely poor saw a significantly greater increase in shoe ownership and insurance expenditure than did the moderately poor, while at endline, the extremely poor had a significantly greater increase in slipper ownership than did the moderately poor. The effect on CHF participation at endline is slightly larger (but not statistically significantly different) for extremely poor households (column 4). However, Panel C reveals that while the increase in use of health insurance at endline was larger for the extremely poor than for the moderately poor, the difference is not statistically significant. Overall, these results suggest that not only can a CCT program increase take-up of products that tend to prevent health problems from occurring and help households cope with health-related risks, but also that in some cases, the poorest of the poor benefit most.

# **6.3 Exploratory analysis: Timing and drivers of health impacts**

Our findings raise two important and related questions that have not been fully answered: First, why do health improvements show up at endline but not at midline? Second, did clinic

> 27 While we find no significant impacts of treatment on other types of providers (columns 3–8), there are two statistically significant differences worth noting. First, at midline, treatment led the moderately poor to increase use of public health centers—though had no significant impact on their use by the extremely poor. Second, at midline, treatment led the extremely poor to decrease use of private dispensaries, hospitals, clinics, and stores—though had no significant impact on their use by the moderately poor.

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conditions contribute to the health improvements realized from the program, or were they unnecessary? We carry out exploratory analyses to shed further light on both questions.

Appendix Figure A2 presents four village-level scatterplots, each containing 80 data points: 40 showing treatment village averages (in black circles), and 40 showing control village averages (in grey squares), with separate linear fits for each set of 40. We plot on the y-axis the average change in the number of sick days in the last month between baseline and follow-up (positive numbers indicate an increase in sick days, negative numbers a decrease). On the x-axis, sub-figure (a) has the village average number of clinic visits per person at baseline, while sub-figure (b) has the share of the village already complying with the health conditions at baseline. Each sub-figure features a plot for each of the two follow-up surveys.

Sub-figures (a) and (b) tell a similar story; reductions in the intensive margin of illness (sick days) show up at midline for a subset of the population (even if there are no significant reductions in the aggregate, as shown in our regressions): those already complying with or exceeding program health conditions at baseline and those with more clinic visits at baseline (call these “the compliers”). This suggests that it was not the conditions driving initial (midline) health improvements; it was the income effect of the transfer on individuals already visiting clinics frequently. However, by endline, the story reverses. It was those who were not complying with the conditions at baseline and those with fewer clinic visits at baseline (call these “the non-compliers”) who saw the greatest reductions in sick days.

Our regressions showed that treatment boosted health clinic visits at midline. Appendix Figure A3 further reveals that this midline increase in clinic visits was larger among noncompliers than among compliers.<sup>28</sup> This suggests that the CCT program helped individuals in two waves. First, compliers experienced a mild reduction in sick days at midline, likely due to income effects of the CCT. Second, non-compliers experienced health benefits, but with a lag. By midline they were induced to increase their health clinic visits—likely due to both the conditions of the program and the income from the transfer permitting them

> 28This is also the case at endline, where despite no aggregate increase in clinic visits at endline due to treatment, we see increases for those with low rates of compliance with health conditions at baseline.

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to go to the clinic when sick rather than allowing illness to go untreated. But it was not until endline that this paid dividends in terms of better health. Indeed, by endline, these non-compliers likely benefited from at least two factors: their increased exposure to clinics at midline as well as the fact that treatment had already reduced illness in a number of children in the village (i.e., the compliers), spurring an overall reduction in infectious disease rates that shows up in our regressions as statistically significant overall impacts of treatment on sick days at endline. Appendix Figure A2 also reveals that we see larger reductions in sick days at endline among those with fewer clinic visits at baseline (sub-figure (a)) and among those with lower rates of compliance with conditions at baseline (sub-figure (b)), consistent with conditions helping to explain overall health improvements.

# **7 Conclusion**

This paper provides evidence that, after 2.5 years, a conditional cash transfer (CCT) program in Tanzania made children aged 0–5 experience fewer monthly sick days. We find no evidence of health improvements for those aged 60 and over despite their having also been required to visit a health clinic as a condition of the transfer, suggesting greater promise of such programs for the young.

The statistically significant improvements in health outcomes after 2.5 years are particularly striking given that the program’s initial effect of increasing annual clinic visits had disappeared after 2.5 years of transfers. If health improvements were not driven by increased clinic visits, then what was the cause? Previous analysis suggests that these study households did not significantly increase consumption (Evans et al., 2014). Instead, we show that households used their transfers to reduce the risk of high heath care costs. Households invested in footwear for their children, which reduces exposure to health risks. Households were substantially more likely to invest in a government-run health insurance program. They went on to utilize that health insurance to finance clinic visits when ill. Although the total 25
number of clinic visits was not higher among beneficiary households, participation in the insurance program meant that those households could attend the clinic when they most needed it, rather than letting immediate financial liquidity determine when, in the course of an illness, to visit the clinic. This is consistent with findings from Adhvaryu and Nyshadham (2015), who demonstrate that households that access formal sector malaria treatment in a more timely way have better health outcomes. The number of visits matters only in part; the timing of visits is also crucial, and the insurance program makes that timing more flexible. Furthermore, the initial increase in visits associated with the program may have increased household familiarity and comfort with clinic services. The availability of such health financing instruments and—potentially—explicitly making them available at the point of transfer distribution may be important considerations if countries desire to fully reap health gains from cash transfers.

Our analysis of the health impacts of Tanzania’s CCT program is not without caveats; while self-reported health measures improved, we do not find enduring impacts on children’s anthropometrics. The cash transfers may make children feel better and be more able to carry out daily activities (e.g., attending school and fetching water), but these may not immediately translate into growth—at least not within 2.5 years. However, they suggest a clear increase in reported child well-being.

We find some evidence that overall, health improvements—at least on the intensive margin—are greater in villages with more health workers per capita. In other words, cash transfers can most effectively reduce the number of days individuals are sick when clinics are sufficiently staffed to provide high-quality services. Clear evidence demonstrates that healthier households are likely to have higher incomes, which then drive better health in a virtuous cycle (Strauss and Thomas, 1998). The evidence from this study demonstrates that supply-side investments (in health care providers) combined with cash transfers (to permit households to insure against health shocks) may be critical catalysts to that virtuous cycle.

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