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Published: December 2012; Last updated: November 2017

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Program description

There are three types of cash transfer programs that have been studied:

• Conditional cash transfers (CCTs), in which recipients receive cash only if they fulfill various requirements such as rates of school attendance or visits to health centers. There is a subset of CCTs in which the conditions are announced but are not formally monitored, so all participants receive a transfer regardless of compliance with the announced conditions.1
• Unconditional cash transfers (UCTs), in which selected participants receive funds without a requirement to meet additional conditions.
• Business grant programs, in which unconditional in-kind or cash grants are given to micro-enterprises that have no paid employees other than the owners.

The program conducted by GiveDirectly is different from most of the cash transfer programs that have previously been studied because it aims to transfer wealth rather than income, and not exclusively to business-owners. In practice, this means that participants receive large sums of money (~100% of per-capita annual consumption) over a relatively short period of time (~8 months), with no formal or informal restrictions on how the funds are used.

We review the results of all three different types of cash transfer programs that have been studied, including a randomized controlled trial of a variant of GiveDirectly's program, in order to address the likely effects of GiveDirectly's cash transfers. In the case of conditional cash transfers, we focus on impacts that do not seem relevant to the conditionality itself, e.g., impacts on consumption rather than on school attendance or other behaviors that are conditions of receiving the transfers.

Program Track Record

Below is a list of the cash transfer programs evaluated by randomized controlled trials (RCTs) that we reviewed for our initial report in 2012.2 This list includes basic information about the program and key findings from the RCT that studied the program. We discuss many of the studies in more detail on our old cash transfer review page. For a list of the studies we identified in our 2013 update of this report, see this footnote.3

A more detailed version of this table is available here (XLS).

How do people spend the money they receive via cash transfers?

GiveDirectly's program is substantially different from nearly all cash transfer programs that have previously been studied. Accordingly, it is not clear that evidence from most academic studies (of very differently-structured cash transfer programs) will provide accurate estimates of the effect of GiveDirectly's cash transfers on their recipients; GiveDirectly's transfers might be either far more or far less effective than more conventionally-structured cash transfers:

• receiving large lump sums might lead people to spend more frivolously; or
• lump sums might be invested at higher rates than ongoing transfers would be, leading to higher long-term consumption.

For this reason, in assessing GiveDirectly's impact, we put the most weight on the results of an RCT of a variant of GiveDirectly's program, discussed below. Despite the questions about the applicability of the evidence from other cash transfer programs to GiveDirectly's programs, we review this evidence below.

Food

Note: the section below was published in December 2012. In the years since, we have searched for additional literature on cash transfers but have not found any studies that substantively changed our views (more on our research process here). Of all the recent literature, we put the most significant weight on an RCT of a variant of GiveDirectly's program. For more on how recipients spent funds in this study, see below.

As discussed at our old in-depth review of cash transfer impacts, most of the studies we have reviewed on cash transfers show meaningful impacts on food consumption (~20% increase over baseline/control group spending on food). In addition, the World Bank's review states, "There is a good deal of evidence that households that receive CCTs spend more on food and, within the food basket, on higher-quality sources of nutrients than do households that do not receive the transfer but have comparable overall income or consumption levels"46 - such as milk, meat, fruits, vegetables, and eggs.47

Across the four randomized controlled trials where it is measured in comparable terms, increases in spending on food makes up more than half of the transfer amount:

• In a randomized study of the Mexican Oportunidades conditional cash transfer program, approximately three quarters of transfers are estimated to be spent on food.48
• A second study from Mexico, of the Programa Apoyo Alimentario, an unmonitored conditional cash transfer, found that nearly all (94%) of cash transfers were spent on food.49
• A randomized study of the RPS conditional cash transfer program in Nicaragua estimated that roughly three quarters of the transfer was spent on food.
  50
• In a randomized controlled trial of the CT-OVC unconditional cash transfer program in Kenya, roughly half of transfers are spent on food.51

Alcohol and tobacco

Note: the section below was published in December 2012. In the years since, we have searched for additional literature on this topic but have not found any studies that substantively changed our views (more on our research process here). Of all the recent literature, we put the most significant weight on an RCT of a variant of GiveDirectly's program, which did not find an increase in spending on alcohol or tobacco. For more on recipients' spending on alcohol and tobacco in this study, see below.

Cash transfers could be used for alcohol or tobacco, which may have adverse effects.

Three randomized controlled trials of cash transfers that report spending on alcohol or tobacco do not find large increases due to cash transfers:

• A randomized study of the Programa de Apoyo Alimentario food security program in Mexico, which had formal conditions that were not enforced, found that cash transfers caused an increase in alcohol consumption equivalent to 1.5% of the value of the transfer, and no increase in tobacco consumption.52 The authors add, "Only 5% of households report consuming alcohol in any amount. This is most likely an underestimate as the survey was usually answered by the female head of the households who might not be aware of all alcohol purchases by other family members. Importantly, given the large increase in consumption of non-alcohol goods under both transfer types, there is little leeway for household members to purchase non-recorded alcohol."53
• In a randomized study of the Nicaraguan conditional cash transfer program Red de Protección Social, alcohol and tobacco made up 0.5% of food expenditures, and the effect of cash transfers was small (0.1% of food expenditures) and statistically insignificant.54 However, this study also states, "Information about alcohol and tobacco expenditures in these types of surveys is often unreliable; it is presented separately and we draw no conclusions from the reported information."55
• A randomized evaluation of Kenya's CT-OVC unconditional cash transfer program found a small and statistically insignificant decrease in alcohol consumption.56

In all three studies, these results come from surveys of how people spend money in general, rather than specifically asking about the spending of cash transfer funds, and then comparing reported spending on alcohol and tobacco across the treatment and control groups. Different forms of misreporting of spending would have different effects on the validity of the estimates, but we would guess that the misreporting would lead the estimated effects to be biased downward (i.e. to underestimate the effect of transfers on alcohol consumption).57

A study by the World Bank, which we haven't looked at closely, reviewed "19 studies with quantitative evidence on the impact of cash transfers on temptation goods [primarily alcohol and tobacco], as well as 11 studies that surveyed the number of respondents who reported they used transfers for temptation goods" and concluded that "Almost without exception, studies find either no significant impact or a significant negative impact of transfers on temptation goods [and in] the only (two, non-experimental) studies with positive significant impacts, the magnitude is small."58

Taking into account the three studies, the review and the potential for bias, we would guess that any increases in consumption of alcohol or tobacco due to cash transfers would be small.

Investment

Note: the section below was published in December 2012. In the years since, we have searched for additional literature on this topic but have not found any studies that substantively changed our views (more on our research process here). Of all the recent literature, we put the most significant weight on an RCT of a variant of GiveDirectly's program. For more on how recipients spent funds in this study, see below.

We have seen five studies examining the extent to which people invest their cash transfers, leading to longer-term gains:

• Gertler, Martinez and Rubio-Codina 2012 is a followup of a randomized rollout of the Oportunidades program in Mexico, in which the treatment group was randomly selected to receive conditional cash transfers a year and a half earlier than the control group. It finds that people in the treatment group saw faster increases in their ownership of farm assets like land, started more microenterprises--“mainly production of handcrafts for sale”--and ultimately saw ~5% higher consumption levels than those in the control group, even four years after the latter had been enrolled in the program.59 The authors estimate that 74% of transfers are consumed and 26% are invested, an estimate that we discuss in more depth below.60 They go on to say:61
  Note that our estimate of the [marginal propensity to consume] MPC is consistent with other estimates in developing countries. For example, Musgrove (1979) estimates MPCs of 0.881 for urban Colombia, 0.896 for urban Ecuador, and, 0.776 for urban Peru; and Bhalla (1979) reports an MPC of 0.61 for rural India. Moreover, its value is relatively high, which is suggestive that beneficiaries are perceiving the program as a permanent—as opposed to transitory—source of income: Paxson (1992) reports MPCs out of permanent income from 0.56 to 0.84, and MPCs out of transitory income ranging from 0.17 to 0.27 for a sample of rice farmers in Thailand.

• A randomized evaluation of the Nicaraguan Red de Protección Social, a conditional cash transfer program, did not find any change in investment (except in human capital) due to the cash transfers.62 However, the authors note that, “households are indeed following the recommendations of the program; that is, they are spending most of their income from the program on current (food and education) expenditures.”63
• A randomized evaluation of the Kenya Cash Transfer for Orphans and Vulnerable Children (CT-OVC), an ongoing unconditional cash transfer program, found that 87% of the transfer was consumed.64 The remaining 13% is not accounted for by the study, but the authors speculate that it may be invested.65 It could also have been saved (without investment), transferred to other individuals, or simply mis-measured.66
• In a randomized study of unconditional grants to micro-enterprises without any paid employees in Sri Lanka, recipients reported that 58% of their unconditional grants were immediately invested in the business, another 12% was saved, and the remaining 30% was spent on household consumption, investment, or other uses.67 Measures of the impact of the grants on capital stock show more dramatic effects, suggesting that cash grants increase capital stock for the recipient's micro-enterprise by as much as 100% of the grant amount.68
• A similar randomized study of unconditional grants to micro-enterprises without any paid employees in Ghana estimated that cash grants to women increased household spending by 50-80% of their value during the quarter following grant receipt and cash grants to men increased household spending by 33-50% of their value, though the estimate for men was not statistically significant. The variation in estimated spending, especially amongst women, arises from very high levels of household spending amongst relatively few individuals, though the results for women remain significant after truncating at various levels.69

  The estimated effects of the cash grants on business capital stock were not statistically significant, but varied between roughly one third and one half of the transfer value for women and between roughly zero and 20% of the transfer value for men, depending on whether full or truncated values were used.70

Note, though, that the cash transfers by GiveDirectly are both larger and made to poorer individuals than any of the transfers discussed above:

• Economic theory and the citations quoted above from Gertler, Martinez, and Rubio-Codina (2012) suggest that larger, shorter term transfers are more likely to be invested than smaller, ongoing transfers, and comparing the results from the ongoing cash transfers and the business grants appears to bear this conclusion out, though the estimates overlap significantly.
• However, there is also a potential tradeoff with beneficiary wealth: poorer recipients are typically expected to consume more of a cash transfer, relative to wealthier individuals. This coincides with our worry that GiveDirectly's focus on targeting the poorest may be systematically targeting individuals who are less likely to invest or, if they do invest, to reap large returns.

What return on investment do cash-transfer recipients earn?

Note: the section below was originally published in December 2012. In September-October 2013, we searched for additional literature on this topic (more on our research process here). Of all the recent literature, we put the most significant weight on an RCT of a variant of GiveDirectly's program in which recipients earned substantially smaller returns. Two other new studies found high returns from unconditional cash grants with features encouraging investment.71 In November 2013, we updated this section to include results from these three studies.

A variant of GiveDirectly

Haushofer and Shapiro 2013, an RCT of a variant of GiveDirectly's program, found that cash transfers increased the likelihood of owning an iron roof by 23 percentage points.72 The study estimated that iron roofs have annual investment returns of 19%, which includes both the savings from no longer having to repair thatched roofs and the savings from no longer having to replace thatched roofs.73 The cost estimates come from a survey of one respondent from each of 20 villages.74

GiveDirectly also conducted a survey on roof costs.75 This survey found costs that imply an annual investment return of 48%.76 We have not been able to resolve this discrepancy.

In addition, Haushofer and Shapiro 2013 Policy Brief estimates an annual investment return of 7% or 14% depending on whether thatched roofs have to be replaced once every 2 years or once a year.77 It does not mention the repair costs associated with thatched roofs, while Haushofer and Shapiro 2013 includes both repair and replacement costs.78 It is possible that these differences account for the discrepancy between the policy brief and the paper, but we are not certain. In any case, the estimates of cost from the policy brief and paper also appear to conflict with GiveDirectly’s survey.

We have not been able to identify the reason for differences between these 3 different estimates. We currently do not have high confidence in the annual investment return calculations in the above sources.

Haushofer and Shapiro 2013 is discussed in much more detail below.

Unconditional wealth transfers with features encouraging investment

Two studies of unconditional wealth transfers in Uganda both found high annual returns of 30%-39% on the original grant.79 Both of these programs included many features designed to encourage investment and improve returns, which distinguish them from GiveDirectly's intervention. The studies are discussed in more detail below.

Conditional cash transfers

The only randomized controlled trial of ongoing cash transfers that discusses the returns that recipients earn on their investments is based on the Oportunidades conditional cash transfer program in Mexico, described above.80 Gertler, Martinez, and Rubio-Codina (2012) estimates that, four years after the control group began to receive treatment and five and a half years after the treatment group began to receive transfers, the treatment group continued to have consumption 5.6% higher than the control group.81 This implies, by our calculation, a 1.7% monthly return, and a 21% annual return, on the transfers,82 which further implies a 3.6% monthly, and 42.6% annual, rate of return on investment.83

Using a different method, Gertler, Martinez, and Rubio-Codina (2012) estimates that for every hundred dollars transferred more than two years ago, recipients continue to earn $1.60 per month in additional income, for an annual return of 19.2%, even though they estimate that only 26% of transfers are invested.84 Since only 26% of transfers are invested, this implies an even higher rate of return on investments, of roughly 75% per year, or 6% per month.85

In these calculations, the authors do not rely purely on the randomized comparison between the treatment and control group. Instead, they estimate current consumption as a result of current and past cumulative transfers, which depend both on the randomized roll-out of the program, and on the number, age, gender, and school attendance of the children in a family. While the number, age, and gender of children are plausibly exogenous (i.e. they are not influenced by current consumption), and thus can just be included in the regressions as controls, the school attendance of children in the family is endogenous: worse school attendance is likely to lead to both decreased transfers (since the conditions punish families for not sending children to school) and increased consumption, since children not in school may be more likely to work.

For exogenous variation in the transfers, the authors use instruments consisting of the maximum amount of transfers that the family could have received had their children had perfect attendance.86 This explains a large portion of the variation in actual transfers received, and is likely exogenous (i.e. maximum potential transfers are likely “as good as random” once family demographics are controlled for, and family demographics are likely not influenced by consumption).

Regressing current consumption on the current transfers and cumulative transfers from previous years, the authors estimate that every $100 in current transfers translates into an additional $48.70 of reported spending during the past month, and every $100 in transfers from more than 2 years ago translates into an additional $1.50 of reported spending during the past month.87 However, this is likely to be an underestimate of the total effect because many students worked, causing both a reduction in transfers for them relative to the maximum possible and an increase in consumption for their families (through their wages).88 By assuming that maximum potential transfers influence current consumption only through actually received transfers, which seems plausible, (i.e. by using maximum potential transfers as an instrument for actual transfers) the authors estimate that $100 of actually received transfers this month increases consumption by $74, and $100 of actually received transfers from more than two years ago increases consumption this month by $1.60.89

The authors pursue this instrumental variables strategy, rather than just regressing current consumption on total realized transfers, because the realized transfers are negatively correlated with consumption because of the child labor effects of conditionality, which would lead to an underestimate of the effects of transfers.

The three different estimates discussed for long-term annual returns on cash transfers are quite similar (20.4%, 18%, 19.2%), though the estimated returns on investment differ significantly (42.6%, 35%, 73.8%), because of different estimates of how much of the transfers are consumed.

Business grants

These estimated returns seem quite high, but there is a separate literature on the returns to capital in micro-enterprises that is relevant to this issue. In a series of experiments in Sri Lanka, Mexico, and Ghana, researchers giving grants on the order of $100 to micro-enterprises without any paid employees have found high returns on investment, in the range of 6%-46% per month:

• A series of papers by de Mel, McKenzie, and Woodruff based on a randomized controlled trial of one-time grants to micro-enterprises in Sri Lanka have found large positive effects on profits for male owners.90 Approximately five years after initially making grants of $100-$200, divided between cash and in-kind gifts, to microenterprises that did not have any non-owner employees, the authors found $8-$12 higher monthly profits in male-owned businesses that received grants.91 This translates to a 6-12% monthly real return amongst male-owned businesses (with no measured benefits amongst businesses owned by women).92 In earlier work covering the first two years after the grants were made, the authors found similar monthly rates of return, and could not reject the hypothesis that cash and in-kind grants had similar effects on profits.93 During the first two years after the grants were made, the combined effect of the cash on men and women was large and statistically significant, though the returns for men were substantially larger than for women,94 but after five years, the combined effect for men and women appears to no longer be statistically significant (this is our conjecture; we cannot confirm it without examining the raw data and calculations for the study, which we have not done).95
• In a similar randomized experiment conducted in Ghana, with a larger sample size and shorter follow-up period, Fafchamps et al. (2011) found comparable large effects on microenterprise profits for in-kind transfers (~20% return per month), but effects on business profits for cash were statistically indistinguishable from zero.96 As discussed above, this may be a result of recipients spending transfers in the household rather than investing in their businesses.
• A similar randomized controlled trial in Mexico, which gave cash or in-kind grants of about $140 to retail micro-enterprises (all owned by men and without paid employees), found returns to capital of 28 to 46% per month over a 3-12 month follow-up period, with indistinguishable differences between cash and in-kind grants.97 The biggest effects (~100% return per month) were concentrated within the 38% of micro-enterprises that were very credit-constrained.98 Although the effects in the credit-constrained subgroup were large and precisely-estimated, the study suffered from substantial attrition (>50% in both treatment and control groups, with similar rates for the two), harming its power and calling the accuracy of the estimates into question.99

RCT of GiveDirectly’s program

We place very high weight on the results of Haushofer and Shapiro 2013, a publicly pre-registered, randomized controlled trial of a variant of GiveDirectly’s program in Rarieda, Western Kenya, because the intervention it evaluated was the most similar to GiveDirectly’s standard program out of all of the RCTs we have seen and because it explicitly addressed issues related to selective reporting bias and multiple comparison problems.100 The trial differed from GiveDirectly’s standard program in one key way: while GiveDirectly currently transfers $1,000 to program recipients, 72% of treatment group members in the evaluation received just $287, less than 30% of the standard amount (one smaller treatment arm did receive $1,085 transfers).101 When interpreting the results, we keep this difference in mind because we believe that the size of a transfer probably has substantial effects on the magnitude of its impact and its effect on recipients’ behavior.

How the program worked

GiveDirectly is an organization that delivers unconditional cash transfers to poor households in Kenya through a mobile money system called M-Pesa.102 While it has altered its model for various experiments, GiveDirectly’s standard model involves transferring $1,000 to poor households, which are identified by their use of thatch roofs.103 Please see our review of GiveDirectly for much more detail on GiveDirectly’s program.

Haushofer and Shapiro 2013’s evaluation of GiveDirectly was randomized on two levels: eligible villages were randomly sorted into treatment and control groups and eligible households within treatment villages were randomized again into treatment households and controls.104 Researchers were therefore able to calculate treatment effects by comparing treatment households to control households within treatment villages.105 They could also calculate the spillover effects the transfers had on non-recipients by comparing control households in treatment villages to otherwise similar households in control villages.106

Different variations of the program were evaluated. Treatment households were cross-randomized into three arms, which varied the gender of the recipient (when households had both male and female household heads), the frequency of the transfer (lump-sum v. monthly installment), and the size of the transfer ($287 v. $1,085).107 The study measured short-term effects of the transfer.108 The time between end-line survey and receipt of final transfer ranged from zero months (for households still receiving transfers when they were surveyed) to fifteen months.109

Effects on GiveDirectly recipients

72% of treatment group households in the evaluation received just $287; the rest received $1,085.110 In the sections below, we use the outcomes from the larger transfer group unless otherwise specified, because GiveDirectly typically gives transfers of similar size.111 For every outcome, the larger transfer led to more spending compared to the smaller transfer with a few exceptions, where we have noted the outcome for the smaller transfer group in the text, and for tobacco and alcohol and indices of health and education, where the effects were not statistically different from zero. Though we report transfer sizes in exchange-rate adjusted terms, we report the outcomes in purchasing power parity (PPP) adjusted U.S. dollars.112

How GiveDirectly transfers were spent

Researchers collected data by surveying members of the treatment and control groups about their recent spending. All data that follows comes from participant self-reports. GiveDirectly recipients increased the value of their non-land assets and their monthly consumption.113 Their spending is broken down in more detail below.

• Total non-land assets.114 Receipt of large transfers increased households’ non-land assets by an average of $463 (95% CI: $378 to $549).115 The largest categories of asset increases were livestock ($131, 95% CI: $79 to $183), durable goods ($100, 95% CI: $71 to $129; primarily furniture), and savings ($18, 95% CI: $9 to $27).116 Households receiving transfers (small or large) were 23 percentage points (95% CI: 17% to 29%) more likely to have an iron roof than the control households.117 Though Haushofer and Shapiro 2013 doesn't report the change in likelihood for recipients of large transfers alone, recipients of large transfers were 23 percentage points (95% CI: 13% to 33%) more likely to have iron roofs at end-line than recipients of small transfers.118 Haushofer and Shapiro 2013 estimated that iron roofs cost about $564 USD PPP based on a survey of one respondent in each of 20 villages.119 GiveDirectly ran a survey that sampled a respondent from each of 20 villages and found that iron roofs cost $418 USD PPP on average.120 We do not know what explains this discrepancy.
• Business expenses. Households receiving large transfers spent about $13 per month (95% CI: $1 to $25) more than control households on business expenses, which were primarily made up of non-durable expenses on non-agricultural businesses.121 Recipients of small transfers also spent about $13 more per month (95% CI: $4 to $22).122
• Health expenditures Recipients of large transfers spent about $3 (95% CI: -$1 to $6) per month more than control households on health expenditures.123 Recipients of small transfers also spent about $3 (95% CI: $1 to $5) more.124 This spending was also included within the estimate of spending on consumption, below.
• Education expenditures. Haushofer and Shapiro 2013 reports that treatment households receiving large transfers spent $1.89 (95% CI: $0.20 to $3.58) more than the control households on education expenditures and treatment households receiving small transfers spent $0.79 (95% CI: -$0.31 to $1.89) more.125 We're not sure of the time period over which this estimate is calculated. Haushofer and Shapiro 2013 also reports that treatment households receiving large transfers spent $16.26 (95% CI: -$6.50 to $39.02) more than control households on education expenditures in the past month and treatment households receiving small transfers spent $19.41 (95% CI: -$12.22 to $44.74) more.126 We're not sure if the difference between the two estimates is due to the difference in the samples used to calculate them (they have different sample sizes) or the different time periods over which they might be calculated or some other explanation.127 Education expenditures were also included within the estimate of spending on consumption, below.
• Consumption. Treatment households consumed about $51 more per month (95% CI: $32 to $70) than control households.128 About half of this additional consumption was on food.129 This additional consumption also included increased spending on social expenditures and various other expenditures.130
• Alcohol and tobacco. Treatment households did not increase their spending on alcohol or on tobacco.131

Impacts of GiveDirectly transfers on recipients

• Food security. At baseline, food security was low among participants.132 Program participants reported a 0.37 standard deviation (95% CI: 0.17 to 0.57) increase in a food security index over controls.133
• Health and education. The study did not detect an effect on indices of health and educational outcomes.134
• Revenue and profits. Receipt of large transfers lead to a $15 per month (95% CI: -$1 to $32) increase in total revenues and receipt of small transfers lead to a $17 (95% CI: $4 to $30) increase but neither resulted in a detectable increase in profits.135 We emphasize that these are very short-run effects and we do not know whether participants’ business investments might lead to profits in the longer run.

Researchers also considered more subjective measures of impact on recipients' quality of life:

• Psychological well-being. Treatment improved an index of psychological wellbeing by 0.45 standard deviations (95% CI: 0.25 to 0.65).136 There was no observable effect on cortisol for the treatment group as a whole although cortisol, an indicator of stress, was slightly lower in the large transfer group than the small transfer group, a difference that was statistically significant at the 10% level when controls were included in the model.137
• Female empowerment. Control households in treatment villages measure 0.23 standard deviations (95% CI: 0.05 to 0.41) higher on an index of female empowerment than control households in control villages.138 This suggests that cash transfers to a village unexpectedly empowered females in both recipient and non-recipient households. The researchers propose potential mechanisms for this effect, but are explicit that these measured results are surprising and warrant further investigation.139 Note that we report this result for the sake of comprehensiveness but would guess that it is more likely to be random than real.

Spillover effects and village-level effects

Update (November 2017): We provide a more recent and detailed discussion of these effects below.

Other than the potential positive effects on female empowerment, Haushofer and Shapiro 2013 found no statistically significant spillover effects (i.e., effects on non-recipient households in recipient villages).140 However, imprecise and statistically insignificant point estimates suggest the possibility of moderate negative effects on non-recipient households.141

The study found no evidence of village-wide impacts on prices, wages, or crime but estimates are imprecise.142

Program variations

The study did not find statistically discernible differences when it varied the gender of the recipient.143 There was some evidence suggesting that recipients of lump-sum transfers were more likely to purchase assets and recipients of monthly installments were more likely to spend their transfers on food.144

Limitations

• Spillover and village-level effects: differences from GiveDirectly’s standard model. Large transfers might have very different spillover effects and village-level effects from small transfers. Spillover effects and village-level effects also might be larger in GiveDirectly’s standard model, where all eligible households in treatment villages receive transfers, than in the RCT, where a control group within the village does not receive transfers.
• Medium and long-term results. Haushofer and Shapiro 2013 is a short-term evaluation of GiveDirectly. We do not know whether the additional consumption enabled by the transfers will persist over the long-term and whether households’ investment in business expenditures might lead to long-term profits.145 The long-term effects of cash transfers are a key question that affects our estimate of the intervention’s cost effectiveness.
• Dynamics of transfers. The dynamics of the program’s effects are particularly difficult to interpret because some households were still receiving payments at the time of the survey while others received their final transfers more than a year prior to the endline survey.146 Haushofer and Shapiro 2013 may have underestimated effects on investment spending and farm revenue by asking backwards looking questions about treatment households’ spending in time periods before some households received their transfers.147
• Data on roofs. Haushofer and Shapiro 2013, an RCT of a variant of GiveDirectly's program, found that cash transfers increased the likelihood of owning an iron roof by 23 percentage points.148 The study estimated that iron roofs have annual investment returns of 19%, which includes both the savings from no longer having to repair thatched roofs and the savings from no longer having to replace thatched roofs.149 The cost estimates come from a survey of one respondent from each of 20 villages.150 GiveDirectly also conducted a survey on roof costs.151 This survey found costs that imply an annual investment return of 48%.152 We have not been able to resolve this discrepancy. In addition, Haushofer and Shapiro 2013 Policy Brief estimates an annual investment return of 7% or 14% depending on whether thatched roofs have to be replaced once every 2 years or once a year.153 It does not mention the repair costs associated with thatched roofs, while Haushofer and Shapiro 2013 includes both repair and replacement costs.154 It is possible that these differences account for the discrepancy between the policy brief and the paper, but we are not certain. In any case, the estimates of cost from the policy brief and paper also appear to conflict with GiveDirectly’s survey. We have not been able to identify the reason for differences between these 3 different estimates. We currently do not have high confidence in the annual investment return calculations in the above sources.
• Lack of statistical power The study included 471 households cross-randomized among three treatment arms, which led to eight possible treatment groups.155 Some treatment arms therefore have fairly small sample sizes (for example, only 128 households received large transfers) and estimates of relative effects of treatment arms are imprecise.
• Self-reporting bias. Outcome data in this study are self-reported, which could lead to positive bias if treatment households sought to please researchers with their use of the transfers. We are especially concerned that treatment households might under-report their use of alcohol and tobacco.
• Positive bias due to negative spillovers. The study estimates treatment effects by comparing treatment households in treatment villages to control households in treatment villages.156 If transfers had negative spillover effects on control households in treatment villages, estimates of their effects on recipients would be overestimated. The researchers address this issue explicitly in their paper.157

Our interpretation of the results

We place high weight on Haushofer and Shapiro 2013 because we believe it is a well-executed, pre-registered RCT and because it directly measures variations on GiveDirectly’s program. We believe that the RCT supports the notion that, in the short-run, participating in GiveDirectly is likely to increase recipients’ assets and consumption.158

Because of the study’s short-term nature, we cannot confidently determine whether recipients’ increased spending on livestock, agriculture, non-agricultural businesses, and (possibly) education have positive returns but, as of the time of the end-line survey, recipients’ additional business spending had not yielded additional profits.159

Conclusion

Haushofer and Shapiro 2013 supports the notion that GiveDirectly has meaningful impacts on asset holdings and consumption for recipients. However, it also provides initial evidence that GiveDirectly recipients are unlikely to invest their transfers in business activities at high returns, as seen in RCTs of programs that provide business training in addition to cash transfers and/or require recipients to propose business plans.

Evidence from two studies of unrestricted wealth transfers

Here we provide more detail on two studies which provided unrestricted cash grants to recipients in Uganda, the Youth Opportunities Program (YOP) (evaluated by Blattman, Fiala, and Martinez 2013) and the Women’s Income Generating Support (WINGS) Program (evaluated by Blattman et al 2013). We discuss these programs in detail because they are the best evidence, other than the RCT of GiveDirectly's program, of the effects of unrestricted wealth transfers to individuals. However, both program differ from GiveDirectly's in key ways including their features that encourage recipients to invest their transfers.

The Youth Opportunities Program in Northern Uganda

How the program worked
In YOP, groups of 10 to 40 young adults aged 16-35 applied for cash grants so that their members could enter skilled trades.160 In general, participants were “young, rural, poor, credit constrained, and underemployed.”161 Groups submitted written proposals and could request up to $1,000 for non-agricultural skills training and start up costs.162 Cash was transferred to bank accounts in the name of treatment groups’ management committees and no restrictions were placed on the money’s use.163 The size of the grants varied widely; the average grant was $382 per capita and 80% of grants were between $200 and $600 per capita.164

How did YOP recipients spend the transfers?

Most groups chose one trade and chose to have all members enter that trade.165 Strong evidence suggests that participants invested a large majority of their funds. At the median, treatment group members estimated that their group and fellow members spent 11% on skills training, 52% on tools, 13% on materials, and 24% shared in cash or spent on other things.166 When asked about their own investments two years after the distribution, treatment group members reported 340 more hours of vocational training than controls, most of which was in tailoring, carpentry, metalwork, or hairstyling.167 On average, treatment group members also reported $219 more in business assets than controls two years after the disbursement, although this difference was reduced to $130 after four years.168

What were the overall effects of YOP?

• Labor supply. Program participants worked 4.1 more hours per week than controls in 2010 and 5.5 more hours per week in 2012.169 In general, participants increased the hours that they spent working in skilled trades to supplement their agricultural income but continued to spend the same amount of time working in agriculture as controls.170
• Return on investment. There is fairly strong evidence that YOP participants received large returns on their investments, leading to higher income than controls in the long-run. Members of treatment groups earned $8.50 more per month than controls in 2010 and $10.50 more per month in 2012.171 Blattman, Fiala, and Martinez 2013 estimate that the increased earnings in 2010 and 2013 represent average annual returns on the original grant of 30% and 39% respectively.172 There is no evidence that treatment group members earned more per hour than control group members, so the return probably comes from increased opportunities to do profitable work.173
• Other impacts. Participation in YOP also lead to increased durable assets, non-durable consumption, and subjective well-being.174 There was no evidence that YOP affected non-economic factors such as kin integration, community participation, community and public good contributions, anti-social behavior, and protest attitudes and participation.175

Limitations

There are some limitations that lead us to exercise caution when applying results from YOP to GiveDirectly’s program.

• Group structure. The group structure of YOP may have acted as a commitment device, leading recipients to invest a greater portion of their grants than recipients of unconditional transfers directly to individuals, like GiveDirectly.176
• Application process. Groups had to apply for grants with a proposal for investing in skilled trades.177 Motivated, patient, or talented individuals may have been more likely to apply and less likely to be screened out, which could have increased the propensity to invest or returns on investment.178 The application process could also have led to more investment through a mental accounting mechanism, by framing the grant in terms of business.179
• Size of grant. YOP grants were, on average, $382 per group member.180 Like GiveDirectly, YOP’s grants are one-time unconditional wealth transfers. However, YOP’s grants are less than 40% of the size of GiveDirectly’s. We do not have a strong intuition about whether this would lead GiveDirectly recipients to invest a larger or smaller portion of their transfers. However, GiveDirectly participants may have lower ROIs if recipients experience diminishing returns on investment.
• Long-run effects and divestment. Treatment members' increased earnings can only be interpreted as return on investment if they are expected to be maintained in the long-run. There is evidence that some recipients divested from their grant over time, which could mean that earning gains were not permanent.181
• Demographic limitations. Program participants were mostly young adults.182 The effects on business assets and earnings largely disappear if the data is reweighted to reflect the demographic distribution of the entire population.183

The Women’s Income Generating Support (WINGS) Program in Northern Uganda

How the program worked

Villages in WINGS were randomly assigned to one of two phases.184 Participants assigned to phase one entered WINGS in mid-2009 and received five days of business skills training, a $150 startup grant (once they had a business plan approved), and follow up visits and advice from AVSI staff.185 Half of phase 1 participants were also randomly assigned to receive business networking training.186 An end-line survey in November 2010 allowed Blattman et al 2013 to estimate the medium-term effects of the full WINGS program by comparing phase 1 villages to phase 2 villages (who had not yet entered the program).187

Phase 2 villages (which served as controls during phase 1) entered WINGS in early 2011.188 To disentangle the effects of the cash grants from the effects of follow-up, researchers randomly assigned one-third of these villages to receive no follow-up.189

In all, 1,800 of the most vulnerable 14-30 year olds in 120 villages in two districts were selected by AVSI and community leaders to participate in WINGS’ two phases.190 “[T]he typical WINGS candidate was a young woman between the ages of 20 and 35, with little or no formal education, low income and limited access to credit.”191

How did WINGS recipients spend the transfers?

Over half of all participants proposed selling mixed items in their AVSI-approved business plans.192 The vast majority of other business involved the selling of livestock, fish, and farm products.193

When participants themselves estimated the proportion of the grant they spent on different categories, those recipients who did not receive follow up from AVSI staff reported that 27% of the grant was spent on business, 15% was spent on long-term consumption, 2% was spent on short-term consumption, and 54% was saved.194 However, when recipients were asked to estimate the cash amount that they spent on their businesses, they reported an average of just $14.50 of business expenditures, suggesting that they spent less than 10% of the grant on business expenditures.195

What were the overall effects of WINGS 18 months after the grants were distributed?

Phase 1 and phase 2 villages were surveyed eighteen months after phase 1 villages entered WINGS (and before phase 2 villages entered).

• Labor supply. Participating in WINGS caused a 61% increase in employment hours, which consisted of a 41% increase in hours spent on subsistence work and a 79% increase in hours spent on market activities.196
• Earnings and return on investment. After subtracting out the effects of follow-up visits by AVSI staff, we estimate that the other components of WINGS increased beneficiaries’ monthly net earnings by an average of about $4.49/month.197 From these earnings numbers we can estimate a mean monthly return on investment of about 3.0% and a mean annual return on investment of about 35.9% on the original $150 grant.198 These calculations are an overestimate of the return on the grant itself, however, because they include the benefits but not the (quite high) costs of services like business skills training, targeting and disbursement, and (for some recipients) group dynamics training.199 We cannot confidently disentangle the effects of the $150 grant from the effects of the add-on services.
• Other economic effects. Participation in WINGS increased short-term spending, wealth, and savings.200
• Inflation, economic externalities, and general equilibrium effects. Researchers surveyed randomly chosen non-participant households in treatment and control villages in order to measure WINGS’ effects on non-participants (who made up 75%-85% of households in treatment villages).201 By going into trade and increasing the supply of scarce goods, WINGS recipients appear to have created slightly lower prices for all village members.202 Blattman et al 2013 suggests that WINGS led to decreased profits for existing microentrepreneurs (through enhanced competition) and increased wages and income for non-participating agricultural workers (through reduced supply of agricultural labor as WINGS participants work less on others households’ plots).203 The published paper on WINGS (Blattman et al 2015) suggests that WINGS had little effect on the incomes or occupational choice of nonparticipating households.204 We have not attempted to reconcile these findings though it seems like the updated analysis makes a weaker claim about negative effects on nonparticipants than the policy report and it strikes us as reasonable to rely on the updated analysis.
• Hostility towards recipients. Overall, recipients report a low level of hostility from their community (such as serious conflicts, insults, harm, or unprovoked aggression), but they do report 38% more hostility than controls.205
• Health and social impacts. Despite large economic returns, WINGS led to few observable medium-run health and social improvements for participants.206

Limitations
There are some limitations that lead us to exercise caution when applying results from WINGS to GiveDirectly’s program.

• Business plan requirement. We are unable to determine the extent to which the requirement to have a business plan approved encouraged participants to invest more money at higher returns than they would have in the absence of such a requirement.
• Disentangling program elements. We are unable to determine the extent to which WINGS’ business skills training and group dynamics training may have contributed to positive outcomes. While we were able to adjust estimated returns to subtract out the effects of follow-up by AVSI workers, doing so also increases our uncertainty about the magnitude of returns.
• Demographics. WINGS participants were chosen as the most vulnerable members of their communities, while GiveDirectly transfers cash to about 40% of the households in a given village.207 This could lead WINGS to have higher returns than GiveDirectly (if the poorest of the poor have the greatest credit constraints and therefore the greatest returns to capital) or could lead GiveDirectly to have higher returns (if the poorest of the poor have worse spending opportunities or make worse spending decisions).
• Grant size. WINGS’ grant of $150 is only 15% the size of GiveDirectly’s $1,000 transfers. This could lead to GiveDirectly recipients achieving a higher or lower return on their transfers than WINGS recipients. This difference could also lead to differing effects on inflation and on village-wide economies.
• Long-run effects and divestment. The longest run effects measured by Blattman et al 2013 were eighteen months. Our return on investment calculations assume that earnings gains sustained over eighteen months are permanent and we would guess that these earnings gains are maintained in the long-term. However, households may gradually divest from their investments, causing temporary earnings gains.
• Conflicting data on investment spending. Blattman et al 2013 measures investment spending in two ways: 1) by asking grant recipients to estimate the portion of their grant that they spent on business expenditures; and 2) by surveying treatment and control households on their expenditures over the course of a month and comparing investment by treatment households against investment by controls.208 These methods result in very different estimates of investment spending, which leave us very uncertain about the proportion of grants that were invested and also decrease our certainty in the reliability of the study’s (self-reported) survey data on the whole.
• Incomplete description of methodology. Blattman et al 2013 is a policy brief and does not contain the complete methodological description that we would ideally like to see in order to evaluate a study. For example, the study does not describe how data on participants’ net earnings or savings are measured. We believe that accurately measuring earnings and savings among the very poor is difficult so our uncertainty about this data somewhat reduces our confidence in our ROI estimates.

Our interpretation of studies of unconditional wealth transfers with features encouraging investment

Together, Blattman, Fiala, and Martinez 2013 and Blattman et al 2013 provide strong evidence that cash grants of about $150 to $600 to groups of poor applicants and to very poor, uneducated women with business training and business plans can lead to high returns in the medium-term. Blattman et al 2013 also provides some of the most relevant evidence we’ve seen suggesting that hostility from neighbors is not a major problem for most recipients of cash transfers and that cash transfers do not cause inflation.

However, Haushofer and Shapiro 2013’s evaluation of GiveDirectly itself found much smaller business returns. We believe that some combination of GiveDirectly’s lack of a business plan requirement, lack of business skills training, and broader age-range of participants is the best explanation for the apparently lower returns earned by its participants. However, it is also possible that the failure to find investment returns was caused by the shorter time horizon of Haushofer and Shapiro 2013 and GiveDirectly participants’ investments may still mature.

Cost-effectiveness of cash transfers

See the most recent version of our cash cost-effectiveness analysis on this page.

In practice, these calculations are sensitive to assumptions, especially regarding:

• the investment returns to cash transfers;
• the subjective assessment of the relative value of averting child mortality and improving incomes for adults.

We estimate that cash transfer programs are in the same range of cost-effectiveness as our other priority programs.

Note that our cost-effectiveness analyses are simplified models that do not take into account a number of factors. There are limitations to this kind of cost-effectiveness analysis, and we believe that cost-effectiveness estimates such as these should not be taken literally, due to the significant uncertainty around them. We provide these estimates (a) for comparative purposes and (b) because working on them helps us ensure that we are thinking through as many of the relevant issues as possible.

Recommendations and concerns

What are the potential downsides of the intervention?

There are a few potential adverse effects of cash transfers:

• Inflation: a sudden injection of cash into an area may cause inflation. We reviewed four randomized controlled trials investigating this issue:
  • In Programa de Apoyo Alimentario, an un-monitored conditional cash transfer program, no significant effect on inflation was found. The researchers used surveys of stores and households to measure prices of goods at baseline and one year after cash transfers began.209 The reported prices were 2.7% higher in villages receiving cash transfers than in control villages after one year, though the increases were not statistically significant.210 We do not have a clear understanding of how the authors picked the prices they reported from the larger universe of prices they collected.211
  • A randomized study of the Oportunidades conditional cash transfer program finds small increases in prices of 5 of 36 food items for sale in treatment villages immediately following deployment of the cash transfers.212 Although the authors do not observe meaningful increases in prices, they do find positive externalities of cash transfers on ineligible families in treatment villages, equivalent to ~10% of consumption (which is about 2/3 of the benefits experienced by the eligible families in the treatment villages).213
  • Blattman et al 2013, the study of WINGS in Uganda, found evidence of a slight decrease in village-wide prices.214
  • Haushofer and Shapiro 2013, the study of a variant of GiveDirectly's program, found no evidence of village-wide impacts on prices, but estimates are imprecise and may not rule out the possibility of substantial inflation.215
• Cash transfers could discourage wage-earning work by adults. If adults can control the distribution of their work and leisure time, cash transfers may lead them to substitute some leisure for work, leading to a decrease in wages earned (but most likely not a decrease in overall income). A World Bank review of the evidence on cash transfers (which we have not vetted) examines this question and concludes that transfers "appear to have had, at most, modest disincentives for adult work"; it discusses 5 studies, of which 4 found no impact along this dimension.216

  Blattman, Fiala, and Martinez 2013 and Blattman et al 2013 both found that cash transfers with features encouraging investment increased hours worked by recipients.217 Haushofer and Shapiro 2013, the study of a variant of GiveDirectly's program, found evidence of a $17/month increase in recipients' total revenue, which suggests that did not decrease their hours worked.218

  Note that there is substantially more evidence suggesting that conditional cash transfer programs lead to reductions in child labor,219 which may help explain the gap between transfer sizes and observed increases in consumption.220

• Giving cash to some and not others could possibly cause social unrest. Haushofer and Shapiro 2013, the RCT of a variant of GiveDirectly's program, found no significant effects of transfers on the rate of crime in treatment villages221 or on instances of physical, sexual, or emotional violence in treatment households as compared to control households in treatment villages.222 In Blattman et al 2013, recipients reported a low level of hostility from their community (such as serious conflicts, insults, harm, or unprovoked aggression), but they do report 38% more hostility than controls.223 We have not seen any other rigorous evidence discussing this issue.
• Diversion of transfers to wealthier individuals. It’s not clear to us whether this problem would be more or less of an issue in the case of cash transfers than in-kind transfers, and we would guess that the extent of the problem depends heavily on the method of making transfers. Our review of GiveDirectly discusses the extent to which this appears to have been a problem in their distributions.

Do cash transfers have negative effects on neighbors of recipients?

Bottom line

There is suggestive evidence that cash transfer programs may have moderate negative short-term effects on the well-being and economic outcomes (e.g., consumption, assets, and business revenue) of non-recipient households living in the same areas as similar households that receive transfers. However, the evidence for these effects primarily comes from studies of a variant of GiveDirectly’s program that may differ from its core program in important ways. We see these potential negative effects as a minor negative update on the expected short-term effects of cash transfers. The long-term effects of transfers on non-recipient households are unclear.

Other sections of this intervention report are relevant when considering the potential spillover effects of cash transfers, such as our discussion of the evidence on inflation due to transfers and the spillover effects of the WINGS program. These analyses generally do not find evidence of inflation or negative spillovers. However, there are other related studies on this topic that we have not yet investigated that appear to find negative spillovers, such as Baird, de Hoop and Ozler 2012.224 We prioritized investigating the studies we discuss below (Haushofer and Shapiro 2013 and Haushofer, Reisinger and Shapiro 2015) because they were done on a variant of GiveDirectly’s program. We may look at other studies on this topic in the future.

GiveDirectly is running an RCT on the macroeconomic effects of cash transfers that may provide higher-quality and more directly applicable information on this issue in the next year.225

Methodology and findings

The RCT of a variant of GiveDirectly’s program, Haushofer and Shapiro 2013, had a two level randomization scheme:226

1. Eligible villages were randomly sorted into treatment and control groups.
2. Eligible households (i.e., households with thatched roofs) within treatment villages were randomized again into treatment households and control households, with roughly half of the eligible households in treatment villages receiving a transfer. Below, we refer to control households in treatment villages as “spillover” households.

Note that we report transfer sizes in exchange-rate adjusted terms, but we report the outcomes in purchasing power parity (PPP)-adjusted U.S. dollars.227

Haushofer and Shapiro 2013 analyzes the effect of the cash transfer program on the well-being and economic outcomes (e.g., consumption, assets, and revenue) of households that did not receive transfers by comparing spillover households that had thatched roofs at endline to control households (i.e., households in control villages) that had thatched roofs at endline.228 It finds small, non-statistically significant, positive spillover effects on well-being and moderate, non-statistically significant, negative spillover effects on consumption, assets, and revenue (more details on these results in the following footnote).229 It finds no evidence of village-wide impacts on prices, wages, or crime, but estimates are imprecise.230

Haushofer, Reisinger and Shapiro 2015 analyzes an additional source of random variation in the original RCT: treatment villages randomly had different average transfer sizes per eligible household because 1) the proportion of eligible households that actually received cash transfers in a village varied from about 40%-75%, and 2) the proportion of recipient households in a village that received large transfers of $1,085 (instead of small transfers of $287) varied from about 0%-57%.231 Haushofer, Reisinger and Shapiro 2015 uses this variation to do a number of complex comparisons; a slightly oversimplified way of describing its methodology is that it compares outcomes of households that received the same amount of money from the program (whether $0, $287, or $1,085) in villages with a smaller average transfer size to outcomes of similar households in villages with a larger average transfer size (see following footnote for a more detailed description of the study’s methodology).232 Using this strategy, it finds:233

• A non-statistically significant, negative effect of increases in neighbors’ wealth (i.e., neighbors in one’s village having a larger average transfer size) on an index of psychological well-being over the study’s full follow-up period (15 months), and a small, statistically significant, negative effect on life satisfaction (one of the five components of the well-being index) over the same period.234
• A moderate, statistically significant, negative effect of increases in neighbors’ wealth on an index of psychological well-being over shorter follow-up periods. Haushofer, Reisinger and Shapiro 2015 does a sub-group analysis in which it analyzes the effect of increases in neighbors’ wealth on well-being in villages that recently received transfers. This analysis finds a statistically significant negative effect on an index of psychological well-being that is larger than the short-term positive effect that the study finds for receiving a transfer, but the negative effect becomes smaller and non-statistically significant when including data from the full 15 months of follow-up (details on the effect sizes in the following footnote).235 The authors interpret these results as implying that cash transfers have a negative effect on well-being that fades over time.236
• Large, statistically significant, negative effects of increases in neighbors’ wealth on economic outcomes (monthly non-durable expenditure (a proxy for consumption), asset holdings, and revenue). For example, interpreted literally, its findings appear to imply that the average increase in village mean wealth ($354) would cause a roughly 30% reduction in spillover households’ asset holdings (see the following footnote for details on other economic results).237 The authors are unsure of the mechanisms for these effects.238

Our analysis of the findings

It is somewhat unclear to what extent both of the above studies of spillover effects apply to spillovers of GiveDirectly’s core program because GiveDirectly’s program (a) always provides transfers to all eligible households (rather than roughly half, as was done in the RCT) and sometimes provides transfers to all households in a village, and (b) provides the same transfer size (large transfers of about $1,000) to all eligible households (rather than only some households, as was done in the RCT).239 These differences lead to the following sources of uncertainty:

• GiveDirectly’s standard practice of providing transfers to all eligible households may be perceived as more fair and therefore may be less likely to have negative effects on well-being; it seems plausible that poor households that lose a lottery to receive a cash transfer would be more upset than households that failed to meet eligibility criteria. In cases where all households in a village receive a transfer there may be less potential for jealousy of neighbors.
• If negative spillover effects scale linearly with the average transfer size, GiveDirectly’s program would cause larger negative spillovers than were found in the RCT (because the average transfer size in the RCT was smaller than the average GiveDirectly transfer).

Overall, there is evidence that increases in average transfer sizes in a village temporarily reduce psychological well-being (on an overall index), and there is weak evidence that effects on people’s life satisfaction last over a slightly longer period (mean follow-up for the GiveDirectly RCT was 4.3 months).240 It seems plausible to us that GiveDirectly’s program would have temporary negative effects on the well-being of households that do not receive transfers. However, we are unsure to what extent the magnitude of the results from Haushofer, Reisinger and Shapiro 2015 would apply to GiveDirectly’s core program because of the important differences between the RCT and the core program. Additionally, we are unsure how to interpret the life satisfaction results found in the study; the authors seem to emphasize this result and argue that life satisfaction is a distinct component of well-being that can be meaningfully analyzed on its own,241 but (a) we do not feel well-positioned to assess this argument, and (b) we worry about drawing too much meaning from one statistically significant result found among a large number of comparisons. All things considered, we see the well-being effects discussed here as a minor negative update on the likely welfare effects of GiveDirectly’s program.

There is suggestive evidence that cash transfer programs have moderate negative effects on neighbors’ economic outcomes over a fairly short time period (the mean follow-up time for the GiveDirectly RCT was 4.3 months).242 Haushofer and Shapiro 2013 finds moderate, non-statistically significant, negative spillover effects on economic outcomes while Haushofer, Reisinger and Shapiro 2015 finds large, significant, negative effects on these outcomes (as a result of having a larger average transfer size in one’s village). The long-term effects of transfers on non-recipient households are unclear; it seems possible that the long-term effects could be either substantially more positive or negative than the short-term effects. Ultimately, we see these results as a minor negative update on the likely economic spillover effects of GiveDirectly’s program.

What versions of the intervention are best?

We have reviewed one RCT comparing physical cash transfers with electronic transfers to a recipient's cell phone.243 The study found that transferring money to cell phones was cheaper than transferring physical cash to individuals, though the initial cost of the cell phones made the cell phone transfer more expensive than handing out cash. Had the study continued longer, the cheaper ongoing costs of the cell phone transfer mechanism would have made up for the higher initial costs.244 The study also finds that recipients of the cell phone transfer recipients had to walk less than 25% as far, on average, as those who received physical cash in order to “cash out” their transfers (0.9 vs. 4.04 km).245 The cell phone transfers also appear to have increased the diversity of crops grown and consumed by people who received them, relative to the “placebo” group that just received physical transfers and a cell phone.246 The study did not find any adverse effects of using cell phone transfers relative to handing out physical cash.

Our process

2012

Initially, we conducted searches on JSTOR and Google Scholar for terms related to cash transfers, especially seeking out systematic reviews, and tracing citations in order to find randomized trials.

We relied particularly heavily on two major literature reviews in our research on CCTs: a World Bank review247 and a Cochrane review.248 Of the literature reviews that we found, we relied on these two because they included a high percentage of RCTs and they presented the data from the studies clearly.

We also searched the World Bank DIME database for relevant studies, discussed with GiveDirectly staff, and added studies as they arose in the process of drafting and updating this report.

2013

Many new studies on cash transfers have been published since December 2012. For this update we have not attempted to thoroughly read all new research published on cash transfers over the course of the last year. We focused on a recently released RCT of a variation on GiveDirectly’s program in Kenya.249

We also looked for RCTs with evidence on programs that were unconditional, large, wealth transfers (the approach taken by GiveDirectly) and research that appeared most likely to affect our views of the evidence for this intervention.

We relied heavily on studies and commentary on cash transfers that were sent to us by people who follow GiveWell. We also looked at the abstracts of studies cited by two papers by Chris Blattman250 , which reported results from experiments involving large, unconditional cash transfers.

In addition, we searched Google Scholar for studies with “cash transfers” in the title from 2011-2013. We listed all randomized controlled trials (RCTs) of cash transfers in a spreadsheet and read the abstract for all studies to try to identify studies that might change our views on the intervention. We also looked for evidence on the propensity to invest cash transfers, returns to investment, inflation, economic effects on non-recipients, spending on alcohol and tobacco, and community resentment or hostility toward recipients.

Changes in our views

In general, the additional evidence we reviewed did not substantively change our assessment of the impact of cash transfers. We found little evidence that cash transfers caused inflation, negative economic effects on non-recipients, recipient spending on alcohol and tobacco, and community resentment or hostility toward recipients.

The most significant updates to the evidence are results from a randomized controlled trial of a variant of GiveDirectly's program in Western Kenya. These results are broadly consistent with results measured in other cash transfer programs, but do suggest that GiveDirectly recipients may earn lower investment returns on their transfers than recipients in previously studied cash transfer programs.

These results are particularly significant because they assess GiveDirectly's program itself. We continue to interpret other evidence for cash transfers cautiously, as most research examines programs that differ from GiveDirectly in that: 1) the transfers are conditional or framed heavily in terms of investment; 2) the transfers are 60% to 90% smaller than GiveDirectly’s; 3) trainings or other services are provided alongside the transfers. We are not aware of any other studies of the propensity to invest large wealth transfers that were not framed as business grants, restricted to participants with investment proposals and/or provided alongside some form of business training or technical assistance.

Studies we considered

A list of the studies reviewed for our initial report in 2012 is available above. A list of the research on cash transfers that we have seen between December 2012 and December 2013 is available at this footnote.251

This list includes all new RCTs we have seen but does not attempt to comprehensively list every non-RCT that has been published, instead focusing on studies most likely to affect our views.

2014

We reviewed a list of studies and articles on cash transfers that we'd come across or were sent to us throughout the year and conducted an informal search for additional studies that might substantively change our view on cash transfers. We did not find any study that passed that threshold and continue to rely on the studies identified in our last review. We think that (a) studies of large, unrestricted cash transfers or (b) studies that rigorously examine the negative effects of cash transfers could potentially change our view.

2015

We primarily searched for new studies on (a) large, unconditional cash transfers and/or (b) the negative effects of cash transfers because we think these are the types of studies that would be most likely to affect our view of GiveDirectly’s program.

New studies on large, unconditional cash transfers

To find new studies on large, unconditional cash transfers, we (a) searched Google scholar for studies published since 2014 that contained the keywords “Haushofer and Shapiro 2013” (without the quotes) or “GiveDirectly”, (b) reviewed studies mentioned in a section of a World Bank blog post on education and cash transfers and (c) reviewed a list of studies sent to us by Paul Niehaus of GiveDirectly. We identified the following papers as warranting further investigation, but all of the studies differed enough from GiveDirectly’s program that they did not substantively change our view:252

• Harris 2015 is an observational study comparing households in Ethiopia that received very large cash transfers (5x annual consumption expenditure on average) as compensation for the government taking a substantial portion of their land (70% on average) to households that did not get their land taken away.253
• Blattman, Jamison and Sheridan 2015 randomly assigned $200 grants (about 3 months wages) to criminally engaged Liberian men (some also received therapy).254
• Emergency Economies 2014 examined a program that provided cash transfers ($575 USD per household over 5 months) to Syrian refugees in Lebanon during the winter.255

We also found a published paper on WINGS (Blattman et al 2015) whereas we previously relied on the policy report (Blattman et al 2013). The updated analysis did not substantively change our view, but we have added a small update from the new analysis about the effects of WINGS on non-participating households in the relevant section above.

Finally, we examined a pilot study run by GiveDirectly, which they had previously sent to us, that randomized young women to receive large, unconditional transfers.256 This pilot study did not substantively change our view because it had a very small sample size, differed from GiveDirectly’s core program, and did not seem to analyze return on investment of transfers.257

New studies on the negative effects of cash transfers

To find new studies on the negative effects of cash transfers, we searched Google scholar for studies published since 2014 with “cash randomized”, “cash randomised”, “cash experimental”, or “cash experiment” (all without the quotes) in the title. We culled the studies based on their titles.258 We skimmed the 5 remaining studies for discussion on any negative effects of the transfer programs.259 We identified one of the studies (White and Basu 2014) as warranting further investigation (based on a cursory look, none of the other studies reported negative effects). White and Basu 2014, which examined the effect of change in payment schedule for a cash transfer program in Peru on expenditures on temptation goods, did not substantively change our view because it did not, in our view, find meaningfully negative effects (see following footnote for details).260

We also looked for discussion of negative effects in the new studies of large, unconditional transfers that we identified as warranting further investigation. None of the studies reported findings on negative effects that substantively changed our view because either (a) they did not find meaningfully negative effects of transfers, or (b) the potential negative effects seemed to be unlikely to apply to GiveDirectly’s program.261

Haushofer, Reisinger and Shapiro 2015 was released after we finished the search described above. We wrote up our view of the study.

For more information on our search for studies, see this spreadsheet.

Other studies

We de-prioritized further investigation of two RCTs examining the effect of cash transfers on cognitive development (Barham, Macours and Maluccio 2013 and Gilligan and Roy 2014), because it seemed that the conditionality (or perceived conditionality) of the transfers in both studies played a key role in the outcomes, which makes these studies less relevant to GiveDirectly’s unconditional transfer program.262

2017

Throughout the year we tracked new literature that might be relevant to assessing the impact of GiveDirectly's cash transfer program by:

• Setting up alerts so that we were notified whenever new studies cited key studies such as Haushofer and Shapiro 2013.
• Reviewing papers that were sent to us or that were discussed by various development economics blogs and social media accounts that we follow.

We did not find any studies that we thought warranted deeper investigation at this time. We would conduct a deeper investigation of a cash transfer study if, based on the abstract, it seemed that it might provide high-quality information about the humanitarian impacts of unconditional cash transfers in contexts similar to those in which GiveDirectly operates.

We did not deeply review studies of other kinds of cash transfer programs because we believed that if a study was not highly relevant to the core parameters driving our cost-effectiveness analysis of GiveDirectly then it was unlikely to affect our decision making in 2017. We also believe that our cost-effectiveness analysis of GiveDirectly is relatively robust since we estimate that a large portion of the humanitarian benefit of the intervention comes from temporarily raising recipients' consumption.

We expect to reevaluate our views on cash transfers when results from a large, new study of GiveDirectly's program are released; this study will assess the general equilibrium effects of cash transfers: see General Equilibrium Effects of Cash Transfers in Kenya, AEA RCT Registry.

We also edited the negative spillovers section of this report because we believe that the previous version of this section provided too many speculative caveats on the findings of potential negative effects. We plan to revisit this evidence in the future alongside the evidence from the general equilibrium study mentioned above to consider whether we should directly factor in negative effects to our cost-effectiveness analysis.

Sources

Supplemental sources

• 1

  See Bono de Desarrollo Humano (BDH) and Programa Apoyo Alimentario in the programs table below.

• 2

  The only program with an RCT that we know about which we left out is a program which gives cash to recipients for going to get the results of HIV tests. See Lagarde, Haines, and Palmer. 2009, Pg 17. The amounts involved were small ($1-$3), so we think this is better understood as “payment for picking up results” than as a kind of cash transfer program.

• 3

  The file is available here.

  This list includes all new RCTs we had seen but does not attempt to comprehensively list every non-RCT that has been published, instead focusing on studies most likely to affect our views.

  The file is broken into three worksheets. "Main set of RCTs" includes the recent studies that have most influenced our views about cash transfers. This sheet primarily consists of studies that clearly contained evidence of: 1) propensity to invest cash transfers; 2) propensity to spend cash transfers on alcohol, tobacco, or other "temptation goods; 3) recipients' returns on investment; 4) hostility or resentment from cash transfers; 5) effects on inflation or village economies, or other economic effects on non-recipients; 6) differing effects between UCTs and CCTs.

  “Useful non-RCTs and comments” includes relevant non-randomized studies, blog posts or commentary.

  “Other results from Google Scholar” contains information from other recent studies of cash transfers that did not strongly affect our overall views. Most of these studies fall into one of a few categories:

  • non-randomized
  • re-analyses of existing data that focus on various potential secondary benefits or costs of cash transfers. There is widely accessible data relevant to some of the biggest public cash transfer programs, leading researchers to test for effects on a very large number of outcomes that were not pre-registered. For example, we have recently seen studies of Progresa/Oportunidades's effects on elderly mortality and child development. We believe that this type of study is more likely to be affected by publication bias/data mining, so we have not carefull reviewed them.
  • studies of CCTs whose results we would not expect to hold for UCTs (primarily studies that report outcomes that are directly related to the conditions placed on recipients).

• 4Fiszbein and Schady 2009, Pg 268.
• 5“Conditions:
  • Health
    • Compliance by all household members with the required number of preventive medical checkups.
    • Attendance of family member older than 15 years at health and nutrition lectures.
  • Education
    • School enrollment and minimum attendance rate of 80% monthly and 93% annually.
    • Completion of middle school.
    • Completion of grade 12 before age 22.”

  Fiszbein and Schady 2009, Pg 268.

• 6

  Transfers represent 20% of baseline per capita expenditures (a measure of consumption) amongst beneficiaries.
  Fiszbein and Schady 2009 2009, Pg 19. Elsewhere, Fiszbein and Schady report figures for Oportunidades as high as 33% and notes, "The transfer amounts as a proportion of per capita expenditures (or consumption) are not the same across all tables in the report because of differences in the surveys used, including their coverage and year." Fiszbein and Schady 2009, Pg 110.

• 7

  Fiszbein and Schady 2009, Pg 212.

• 8Fiszbein and Schady 2009, Pg 264.
• 9“Conditions:
  • Health: Compliance with required frequency of health center visits; compliance enforced only in the 4 departments where PRAF is supported by the IDB; in the remaining 13 departments, households are encouraged only to send children to school/take them for health visit.
  • Education
    • School enrollment
    • Regular school attendance of at least 85%.”

  Fiszbein and Schady 2009, Pg 264

• 10Transfers represent 9% of baseline per capita expenditures (a measure of consumption) amongst beneficiaries. Fiszbein and Schady 2009, Pg 19.
• 11Fiszbein and Schady 2009, Pg 212.
• 12 Fiszbein and Schady 2009, Pg 272.
• 13 “Conditions:
  • Health
    • "Bimonthly health education workshops (all households).
    • Attendance at prescheduled health care visits every month (aged 0–2) or bimonthly (aged 3–5), adequate weight gain and up-to-date vaccinations (aged 0–5) for all households with children aged 0–5.
  • Education
    • Enrollment in grades 1–4 for children aged 7–13
    • Regular attendance of 85% (that is, no more than 5 absences without valid excuse every 2 months)
    • Grade promotion at end of school year.”

  Fiszbein and Schady 2009, Pg 272.

• 14Transfers represent 27% of baseline per capita expenditures (a measure of consumption) amongst beneficiaries. Fiszbein and Schady 2009, Pg 20.
• 15 Fiszbein and Schady 2009, Pg 212.
• 16Fiszbein and Schady 2009, Pg 270.
• 17“Conditions:
  • Education
    • Enrollment in grades 1–6 for children aged 7–15
    • Regular attendance of 85%, (that is, no more than 5 absences without valid excuse every 2 months)
    • Deliver teacher transfer to teacher.
  • Other
    • For occupational training: household needed to decide on member who takes course, and payment is conditional on attendance at course.
    • For the business grant: business plan approved by technical team in the Ministry of Family”

  Fiszbein and Schady 2009, Pg 270.

• 18Transfers represent 18% of baseline per capita expenditures (a measure of consumption) amongst beneficiaries. Fiszbein and Schady 2009, Pg 20.
• 19Fiszbein and Schady 2009, Pg 212.
• 20Fiszbein and Schady 2009, Pg 258.
• 21 “Conditions:
  • Health
    • Children aged 0–5: bimonthly visits to health posts for growth and development checkups and immunizations.
  • Education
    • School enrollment for children aged 6–15
    • School attendance at least 90% of school days
    • Must be enrolled in school and have attendance at basic education classes of at least 80% (including both justified and unjustified absences).”

  Fiszbein and Schady 2009, Pg 258.

• 22 Transfers represent 10% of baseline per capita expenditures (a measure of consumption) amongst beneficiaries. Fiszbein and Schady 2009, Pg 19.
• 23Fiszbein and Schady 2009, Pg 212.
• 24Dates not listed in study. Skoufias, Unar, and González-Cossío 2008
• 25

  "Localities were randomly assigned into three treatment groups and one control group. Two of the treatment groups were assigned to receive food transfers with and without receiving a health and nutrition education package, and a third to a cash transfer of equal value to the food basket plus the education package...The PAL program offers nutrition and health education sessions (platicas), as well as participation in program-related logistic activities. However, given that attendance of the platicas is not a requirement for the receipt of the benefits, the PAL program is essentially an unconditional transfer program...” Skoufias, Unar, and González-Cossío 2008, Pgs 8-9.

• 26

  Skoufias, Unar, and González-Cossío 2008, Pg 15.

• 27“Both the in-kind and cash transfers were, in practice, delivered bimonthly, two monthly allotments at a time per household. The transfer size was the same for every eligible house- hold regardless of family size. Resale of in-kind food transfers was not prohibited, nor were there purchase requirements attached to the cash transfers. As mentioned above, the monthly box of food had a market value of about 206 pesos in the program villages, and the cash transfer was 150 pesos per month, based on the government’s wholesale cost of procuring the in-kind items.” Cunha, De Giorgi and Jayachandran 2011. Pg 13.
• 28

  Baird, McIntosh, and Ozler 2011.

• 29
  • “Monthly school attendance for all girls in the CCT arm was checked and payment for the following month was withheld for any student whose attendance was below 80% of the number of days school was in session for the previous month.” Baird, McIntosh, and Ozler 2011, Pg 9.
  • “In the UCT EAs, the offers were identical with one crucial difference: there was no requirement to attend school to receive the monthly cash transfers.” Baird, McIntosh, and Ozler 2011, Pg 9.

• 30

  “The average offer to the households consisted of $10/month – for a total of $100 for the school year transferred in equal amounts for 10 months. $10/month represents roughly 15% of total monthly household consumption in our sample households at baseline, which places this program in the middle-to-high end of the range of relative transfer sizes for conditional cash transfer programs elsewhere.” Baird et al. 2009, Pg 12.

• 31

  “The cash payments take place monthly at centrally located and well-known places, such as churches and schools.” Baird et al. 2009, Pg 13.

• 32

  The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on human capital.

• 33

  “Total adjusted mean monthly spending is Ksh 1442 at baseline among T households, or approximately US$18 per month and 60 US cents per day per adult equivalent. Although total adjusted expenditures are similar across T and C households at baseline, the value among T households at follow-up is about Ksh 253 greater – this is consistent with the size of the transfer, which averages Ksh 300 per household in 2007 Ksh.” The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on household spending, pg 14. 300/1442 = 20.8%

• 34“Eligible households, those who are ultra-poor and contain an OVC, receive a flat monthly transfer of US$21 (this was increased in the 2011/12 budget from Ksh 1500 to Ksh 2000).” The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on household spending Pg 11.
• 35
  • de Mel, McKenzie, and Woodruff 2008.
  • de Mel, McKenzie, and Woodruff 2012.

• 36

  “Cash treatments were given without restrictions. Those receiving cash were told that they could purchase anything they wanted, whether for their business or for other purposes. In reality, the grant was destined to be unrestricted because we lacked the ability to monitor what recipients did with the funds, and because cash is fungible. Being explicit about this was intended to produce more honest reporting regarding use of the funds.” de Mel, McKenzie, and Woodruff 2008 Pg 1337.

• 37

  Mean grant as a percentage of mean annual business profit. Mean grant was 15,000 LKR; mean real profits in March 2005 were 3,851 LKR (de Mel, McKenzie, and Woodruff 2008, Table 1). 15,000/(12*3851) = 32.46%.

• 38

  “Firms were told before the initial survey that we would survey them quarterly for five periods, and that after the first wave of the survey, we would conduct a random prize drawing, with prizes of equipment for the business or cash. The random drawing was framed as compensation for participating in the survey. We indicated to the owners that they would receive at most one grant. For logistical reasons, we distributed just over half the prizes awarded after the first wave of the survey, and the remaining prizes after the third wave; enterprises not given a prize after the first wave were not told whether or not they had won one of the prizes to be awarded in the second distribution until after the third wave. The prize consisted of one of four grants: 10,000 LKR (∼US$100) of equipment or inventories for their business, 20,000 LKR in equip- ment/inventories, 10,000 LKR in cash, or 20,000 LKR in cash. In the case of the in-kind grants, the equipment was selected by the enterprise owner and purchased by our research assistants.5 Subsequently, we received funding to extend the panel to nine waves. Because this represented an extension of the survey rela- tive to what firms were told before the baseline survey, we granted each of the untreated firms 2,500 LKR (~US$25) after the fifth wave. The randomization was stratified within district (Kalutara, Galle, and Matara) and zone (unaffected and indirectly affected by the tsunami). Allocation to treatment was done ex ante among the 408 firms kept in the sample after the baseline survey.6 A total of 124 firms received a treatment after wave 1, with 84 receiving a 10,000-LKR treatment and 40 receiving a 20,000-LKR treatment. Another 104 firms were selected at random to receive a treatment after the third survey wave: 62 receiving the 10,000-LKR treat- ment and 42 the 20,000-LKR treatment. In each case, half the firms receiving a treatment amount received cash, and the other half equipment.” de Mel, McKenzie, and Woodruff 2008.. Pgs 1335-1336.

• 39

  Fafchamps et al. 2011.

• 40

  Mean grant as a percentage of mean annual business profit. Mean grant was 150 cedis; mean profits in the trimmed sample at baseline are 106 cedis per month (= (103+99+115)/3) (Fafchamps et al. 2011 Table 1). 150/(12*106) = 11.83%.

• 41

  “We also randomly selected when firms would receive their grant, staggering the timing of the grants, so that 198 firms were assigned to receive the grants after the second round, a further 181 firms assigned to receive the grants after the third round, and 18 firms were assigned to receive the grants after the fourth round. This staggering was done both for the purpose of managing the logistics of making these grants, and to provide incentives for firms to remain in the study for multiple rounds since they were told more grants would be given out after rounds 3 and 4. These grants were framed to firms as prizes to thank firms for participating in the survey. Participants in the survey were told that we were undertaking a study of small firms in Ghana, and that some of the firms would be randomly chosen to receive prizes as a token of our appreciation for their participation in the survey. Firms which were selected in either treatment group were not told they had been selected for a prize until the time their prize was being given out.” Fafchamps et al. 2011. Pg 16.

• 42

  McKenzie and Woodruff 2008.

• 43

  “Cash was given without restrictions on its use. Owners were allowed to contribute funds of their own to purchase items costing more than 1,500 pesos (in practice none did).” McKenzie and Woodruff 2008. Pg 467.

• 44

  Mean grant as a percentage of mean annual business profit. Grants are 1,500 pesos; mean baseline profits are 3,373 pesos per month (= (3433+3312)/2) (McKenzie and Woodruff 2008 Table 2). 1500/(12*3373) = 3.71%

• 45

  “Before the first round of the survey, firms were told that the only compensation that they would receive for participating was a chance of receiving either cash or capital through prizes to be given after each survey round.6 The prize was a grant of 1,500 pesos (about $140). After the first round of the survey, a single draw from a computerized random number generator was used to randomly assign firms to treatment and control groups.7 Among the firms assigned to treatment status, the random draw also determined the round in which they would be treated and whether they would receive their grant as cash or capital for their enterprise. The results of the initial random draw were not revealed to either the survey company or the firms in the sample. After each round, the survey company was given a list of firms to which to distribute the grants. Each firm could receive a prize at most once, although this was not made explicit to the firms.” McKenzie and Woodruff 2008. Pg 466.

• 46

  Fiszbein and Schady 2009, Pg 16.

• 47

  "The increase in expenditures on food generally is directed toward increasing quality. Households that benefi ted from Familias en Acción in Colombia signifi cantly increased items rich in protein, such as milk, meat, and eggs (Attanasio and Mesnard 2006); and the increases in food expenditures in Mexico and Nicaragua were driven largely by increased consumption of meat, fruits, and vegetables (Hoddinott, Skoufias, and Washburn 2000; [Maluccio and Flores 2005]). Oportunidades also increased caloric diversity as measured by the number of different food-stuffs consumed. At similar overall food expenditure levels in Nicaragua, [Macours, Schady, and Vakis 2008] shows that households that receive transfers from the Atención a Crisis program spend significantly less on staples (primarily rice, beans, and tortillas) and significantly more on animal protein (chicken, meat, milk, and eggs), as well as on fruits and vegetables [Angelucci and De Giorgi 2009] and [Attanasio, Kugler, and Meghir 2008] report similar results using data for urban Oportunidades in Mexico. Not only did households diversify their diets; they also shifted toward higher-quality sources of calories." Fiszbein and Schady 2009, Pg 113.

• 48

  Angelucci and De Giorgi 2009. Table 1, Pg 30. May 1999 treatment effect is 24 pesos of additional food per adult equivalent. This amounts to roughly three quarters of the mean transfer: “The actual monthly grants up to November 1999 are sizeable, averaging 200 pesos per household, or 32.5 pesos per adult equivalent.” Pg 6.

• 49

  Mean 4.07 adult equivalents per household (Cunha 2011, Table 2. Pg 37). Cash transfers 150 pesos per month (Cunha 2011. Pg 10). Cash transfers are estimated to increase food consumption by 34.72 pesos per adult equivalent per month (Cunha 2011 Table 4. Pg 39). 4.07*34.72/(150)= 94%.

• 50

  “Over the 2 years, the actual average monetary transfer (excluding the teacher transfer) was approximately C$3,500 (US$272 or 17 percent of total annual household expenditures).” Pg 8. Estimated impacts on total spending at the household level are 2,817 Cordoba (Table 4.1, Pg 27), or 80% of the transfer. The mean per capita increase in total household expenditures is 686 Cordoba (Table 4.2, Pg 29), and the mean per capita increase in total food expenditure is 640 Cordoba (Table 4.3, Pg 30), or 93% of the increase in spending. 93%*80% = 75%. Maluccio and Flores 2005
  

• 51

  The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on household spending,

  • “[T]he size of the transfer... averages Ksh 300 per household in 2007 Ksh.” Pg 14.
  • “Results from this estimation of programme impacts, without con- trolling for the change in total expenditure induced by the programme, are shown in the odd-numbered columns in Table 2, Panel A. These show statistically significant impacts of the programme expenditures for food (Ksh 145), health (Ksh 39), and clothing (Ksh 25).” Pg 16.
  • 145/300 = 48%

• 52
  • “For alcohol consumption, while both [in-kind and cash transfer] treatments induced statistically significant increases (1.73 pesos per [adult equivalent] under in-kind transfers and 2.89 under cash) they are also indistinguishable from each other.” Cunha 2011, Pg 22.
  • For tobacco, see Cunha 2011, Table 5.
  • The total cash transfer equivalent is 193 pesos, so to estimate the increase in alcohol consumption as a portion of the transfer we take 2.89/193 = 1.5%. See Cunha 2011, Pgs 14-15.

• 53

  Cunha 2011, Pg 22. In particular, as indicated above, food consumption was reported to increase by 94% of the total transfer amount.

• 54

  Maluccio and Flores 2005, Pg 32. Table 4.5.

• 55

  Maluccio and Flores 2005, Pg 32.

• 56

  The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on household spending, Pg 13. Alcohol and tobacco consumption goes from .4% of consumption at baseline to .2% at follow-up in the treatment group, while going from .3% to .2% in the control group so the cash transfers are actually estimated to reduce alcohol and tobacco consumption, though the estimate is not statistically significant. (This is not due to an overall increase in consumption; the same pattern holds in absolute currency terms.)

• 57

  Three possible forms of misreporting would have different effects:

  • Simple linear underestimates: if everyone under-reported alcohol consumption by a fixed amount (e.g. $1), then the estimated effect of transfers on alcohol consumption would be unbiased, though they would be upward-biased as a proportion of baseline alcohol consumption.
  • Simple geometric underestimates: if everyone underreported alcohol consumption by a certain proportion (e.g. half), then absolute estimates of the impact of cash transfers on alcohol consumption (including the estimate that 1.5% of transfers were spent on alcohol in the Programa de Apoyo Alimentario food security program in Mexico) would be biased downwards. The estimated proportional increase (e.g. recipients of transfers spent twice as much on alcohol as the control group) would likely continue to be unbiased. This strikes us as the most likely form of measurement error.
  • Transfer recipients underestimate asymmetrically: if transfer recipients recognize that a study is attempting to measure the impact of their transfers on alcohol consumption and therefore lie about alcohol consumption while the control group is truthful, then the estimates would be biased downward in unpredictable ways.

• 58
  • "This paper reviews 19 studies with quantitative evidence on the impact of cash transfers on temptation goods, as well as 11 studies that surveyed the number of respondents who reported they used transfers for temptation goods. Almost without exception, studies find either no significant impact or a significant negative impact of transfers on temptation goods. In the only (two, non-experimental) studies with positive significant impacts, the magnitude is small. This result is supported by data from Latin America, Africa, and Asia. A growing number of studies from a range of contexts therefore indicate that concerns about the use of cash transfers for alcohol and tobacco consumption are unfounded." Evans and Popova 2014, Pg. 1
  • "In this study, we use the term 'temptation goods' principally to refer to alcohol and tobacco…Although alcohol and tobacco are the principal goods under consideration, some studies report other items as part of the same category, from doughnuts (Aker 2013) to soft drinks and Chinese food (Dasso and Fernandez 2013)." Evans and Popova 2014, Pg. 2

• 59

  "We test this hypothesis using data from a controlled randomized experiment of the Oportunidades CCT program in Mexico. We find that beneficiary households increased ownership of productive farm assets, such as farm animals and land for agricultural production, significantly faster than nonbeneficiary households; that agri -cultural production in terms of both crops and animal products increased faster for beneficiary households than nonbeneficiary households; and that this resulted in sig -nificantly higher agricultural income. In fact, we estimate that an 18-month exposure to the program resulted in a 9.6 percent increase in agricultural income. Beneficiary households also started substantially more nonagricultural microenterprises, mainly production of handcrafts for sale, compared to nonbeneficiary households … We then explore whether returns on these investments persist over time and raise long-term living standards as measured by consumption. We find that even 4 years after households in the control group were incorporated into the program, consumption levels for the original treatment households were 5.6 percent higher than for the original control households. This result suggests that returns on investments made by treatment households during the initial 18-month experimental period did in fact translate into improvements in long-term living standards." Gertler, Martinez and Rubio-Codina 2012, Pg 2.

• 60

  In this case, investment is defined as anything that is not consumed in the current period. Gertler, Martinez and Rubio-Codina 2012. Pg 183. “In this section, we estimate how much of the transfer is consumed versus invested—i.e., the marginal propensity to consume (MPC), and the return on transfers in terms of long-term consumption via the investment pathway, which we call the marginal investment effect (MIE). The MPC and the MIE characterize two principal pathways through which transfers affect living standards. First, households can increase living standards in the short run by spending part of the current cash transfer. This amount is just the marginal propensity to consume transfers. Transfers not consumed are saved or invested, so that the marginal propensity to invest transfers is equivalent to (1–MPC).” It is not clear from the paper whether investment in household improvement, such a purchasing a new roof, is considered consumption or investment.

• 61

  Gertler, Martinez and Rubio-Codina 2012, pg 189.

• 62

  Investment in this context is defined as both in terms of specific spending activites (e.g. related to agriculture, home business, and durable goods) and as anything not consumed in the current period; both find limited to no effects:

  • “The study also asked about other forms of expenditures related to investments at the household level, such as on household improvements, durable goods, and so forth; none of these showed significant changes. Finally, we examine expenditures on other specific non-food items including books, furniture, child clothing, remittances sent, lotteries, and parties, and find no significant program effects. Naturally, since total expenditures were flat while the percentage spent on food remained the same, it was unlikely that investments or expenditures like these would have changed very much. It is important to emphasize that the evidence indicates that households are indeed following the recommendations of the program; that is, they are spending most of their income from the program on current (food and education) expenditures. (35) This finding is somewhat weaker in the second year, however, where increased expenditures appear to be slightly smaller than the transfers. It is possible that any differences are relected in increased savings (or increased leisure, discussed later), although we do not have the information to verify this.” The footnote says, “(35) Information on savings is not available so it is not possible to assess whether there was increased savings. Given the evidence on expenditures relative to the transfer size, however, any such increase was likely to be small.” Maluccio and Flores 2005 pgs 32-33.
  • “In years when transfers were being given, the programme increased expendi- tures, and the lion’s share of the increase was on food and educational expenditures. These findings are consistent with the programme’s orientation toward increasing current expenditures (one of its three key objectives) and the required conditions, as well as with evidence from a variety of settings that resources in the hands of women are more likely to be directed to these types of expenditures. With those findings, I turned to an assessment of the programme on investment of various types. Overall, there was only limited evidence that the programme led to increases in the agricultural and non-agricultural types of investment considered. These results are corroborated by a separate analysis estimating a consumption equation, which demonstrated that even though the transfers were to last only for three years and thus were transitory, the average MPC out of transfers was approximately one. Moreover, cumulative past transfers had no effect on current expenditures.
    The findings do not imply that the programme had no long-term effects – it very likely did via increased investment in child health and education, which should continue to lead to benefits for many years to come. In contrast to PROGRESA in Mexico, where there seems to have been substantial agricultural investment and returns from it (Gertler et al., 2007; Todd et al., 2010), there is only weak evidence that RPS increased these other investments in the rural localities in which it operated.” Maluccio 2010, Pgs 34-35.

• 63

  Maluccio and Flores 2005 Pg 33.

• 64
  • “The last column in Table 4, Panel A sums up the ex-ante and ex-post effects; the ex-ante effects suggest that about Ksh 7 out of the total transfer is spent on non-consumption expenditures, possibly investments, while the actual impacts suggest a much larger Ksh 40 (or 13 per cent of the transfer value) goes to non-consumption uses.” The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on household spending, Pg 23.
  • “Total adjusted mean monthly spending is Ksh 1442 at baseline among T households, or approximately US$18 per month and 60 US cents per day per adult equivalent. Although total adjusted expenditures are similar across T and C households at baseline, the value among T households at follow-up is about Ksh 253 greater – this is consistent with the size of the transfer, which averages Ksh 300 per household in 2007 Ksh.” The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on household spending Pg 14.
  • Note that the actual transfer size is 1,500 Ksh per household, but the figures given in the article are per adult equivalent. “Eligible households, those who are ultra-poor and contain an OVC, receive a flat monthly transfer of US$21 (this was increased in the 2011/12 budget from Ksh 1500 to Ksh 2000).” The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on household spending Pg 11.
  • It is unclear whether household improvements, such as a new roof, would be treated as consumption by the study. The section on spending on housing seems to imply that it may only include water and utilities. The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on household spending Pg 12.

• 65

  “The last column in Table 4, Panel A sums up the ex-ante and ex-post effects; the ex-ante effects suggest that about Ksh 7 out of the total transfer is spent on non-consumption expenditures, possibly investments, while the actual impacts suggest a much larger Ksh 40 (or 13 per cent of the transfer value) goes to non-consumption uses.” The Kenya CT-OVC Evaluation Team. The impact of the Kenya Cash Transfer Program for Orphans and Vulnerable Children on household spending Pg 23.

• 66

  If, for instance, the treatment and control group systematically underreported spending by a uniform proportion, there would be a gap between the estimated consumption increase and the transfer size of at least that proportion.

• 67

  “Cash treatments were given without restrictions. Those receiving cash were told that they could purchase anything they wanted, whether for their business or for other purposes. In reality, the grant was destined to be unrestricted because we lacked the ability to monitor what recipients did with the funds, and be- cause cash is fungible. Being explicit about this was intended to produce more honest reporting regarding use of the funds. In the survey subsequent to the treatment, we asked how they had used the treatment. On average, 58% of the cash treatments was invested in the business between the time of the treatment and the subsequent survey. An additional 12% was saved, 6% was used to repay loans, 5% was spent on household consumption, 4% was spent on repairs to the house, 3% was spent on equipment or inventories for another business, and the remaining 12% was spent on “other items.” Of the amount invested in the enterprise, about two-thirds was invested in inventories and the rest in equipment.” McKenzie and Woodruff 2008 Pg 1337.

• 68

  de Mel, McKenzie, and Woodruff 2008,online appendix, Table A4. With no trimming of capital stock, grants are found to increase capital stock by more than 100% of their value (107-115%); after trimming the top and bottom 1% of capital stocks, grants are estimated to increase capital stock by 62-87% of their value. “The first column of the table verifies that the treatment did increase capital stock as intended. All four treatments are significantly associated with higher levels of capital stock. The measured impact of the cash treatments is somewhat higher than the impact of the in-kind treatments, though the large standard errors on the individual treatments mean that the differences between cash and in-kind treatments are not significant. Trimming the top and bottom 1% of capital stock reduces these differences.11” Pgs 1341-42. Footnote 11 says: “The treatment effects after trimming capital stock are 5,780 (6,227) for the 10,000 LKR in-kind (cash) treatment and 13,443 (17,325) for the 20,000 LKR in-kind (cash) treatment.”

• 69

  Fafchamps et al. 2011. “The remaining columns report the estimated impacts on household expenditure, which was collected each wave. Point estimates suggest higher positive impacts on expenditure for those receiving the cash treatments than those getting the in-kind treatment or the control group, especially for women with low initial profits. We see a large and highly significant effect of the cash treatment on total quarterly spending for women as a whole, and for the subgroup of women with low initial profits. The coefficients are huge: women who were given a 150 cedis cash grant are estimated to be spending 120 cedis more a quarter after the grant. The magnitude of this coefficient appears to be driven by a few firm owners reporting very large spending levels — truncating at the 99th percentile of total expenditure lowers this coefficient to 95, and at the 95th percentile lowers it to 76 cedis (which is still significant at the 5% level). For males receiving the cash treatment, the point estimates also suggest large increases in total quarterly spending (with a coefficient of 50 to 73 cedis depending on the level of truncation), but the standard error is so large that we can never reject equality with zero.” Pgs 28-29.

• 70

  Fafchamps et al. 2011. Table 5, columns 1 and 2, Pg 53. Capital stock for women increased by 49.17-82.61 cedis, while capital stock for men increased by 2.21-31.36 cedis, both on a grant of 150 cedis.

• 71

  See the Youth Opportunities Program evaluated by Blattman, Fiala, and Martinez 2013 and the Women's Income Generating Support Program evaluated by Blattman et al 2013.

• 72

  "In particular, we find increases in holdings of home durables (notably metal roofs, ownership of which increased by 23 percentage points over a control group mean of 16 percent), and productive assets such as livestock, whose value increases by USD 85 over a control group mean of USD 167." Haushofer and Shapiro 2013, Pg. 3
  

• 73

  Annual investment return = $107/$564 = 19%. Haushofer and Shapiro also report an internal rate of return (IRR), or the annual discount rate such that the net present value of the investment returns equal the cost of the investment (i.e. the sum of $107/(1 + IRR)^t from t = 0 to t = Infinity equals $564), of 23%. "We therefore next quantify the returns to these investments. To this end, we conducted a separate survey of one respondent from each of 20 villages to obtain estimates for the costs of purchasing and maintaining metal and thatch roofs. The purchase of a metal roof represents an expenditure of on average USD 564, or 75 percent of the average transfer value. In addition to a store of value (roofs can be resold), a metal roof provides an investment return to households by obviating the need to replace and repair their thatched roofs, which costs on average USD 107 per year. Together, these figures imply a simple return on the investment in the roof of 23 percent (assuming no depreciation of metal roofs; this assumption is reasonable as most respondents were unable to put an upper bound on the durability of metal roofs)." Haushofer and Shapiro 2013, pg. 34

• 74

  "To this end, we conducted a separate survey of one respondent from each of 20 villages to obtain estimates for the costs of purchasing and maintaining metal and thatch roofs." Haushofer and Shapiro 2013, pg. 34

• 75

  "GiveDirectly conducted a survey of 20 random CT recipients from 20 different villages. The sampling method entailed calling one person at random in each of the randomly selected villages until someone answered the phone and was able to provide answers to the survey questions." GiveWell's non-verbatim summary of a conversation with Carolina Toth, GiveDirectly, October 1, 2014

• 76
  • ($95+$107)/$418 = 0.48. "Based on the anonymized individual-level survey data, an iron roof costs $418 on average, thatch roof replacement (including the cost of grass for making the roof and the labor) costs $95 on average, and thatch roof repair (including the cost of grass for making the roof and the labor) costs $107 on average. These numbers appear to conflict with the full paper and the policy brief. It may be that the results were from a different survey. Haushofer and Shapiro have not yet finished verifying which data were used." GiveWell's non-verbatim summary of a conversation with Carolina Toth, GiveDirectly, October 1, 2014
  • Note that the cost the survey found for thatch roof repair was the same as the repair and replacement costs in Haushofer and Shapiro 2013: "The purchase of a metal roof represents an expenditure of on average USD 564, or 75 percent of the average transfer value. In addition to a store of value (roofs can be resold), a metal roof provides an investment return to households by obviating the need to replace and repair their thatched roofs, which costs on average USD 107 per year." Haushofer and Shapiro 2013, pg. 34

• 77

  Haushofer and Shapiro 2013 Policy Brief estimated an annual investment return of 7% (($77/2)/$564) or 14% ($77/$564): "Cash transfers increase the likelihood of having an iron roof by 23 percentage points relative to a control group mean of 16%. The purchase of an iron roof represents an expenditure of approximately KES 35,220 (USD 402, PPP 564), or 75% of the average transfer value. In addition to a store of value (roofs can be resold), an iron roof potentially provides an investment return to households by obviating the need to periodically replace their thatched roofs, which must be done ever 1 to 2 years, costing approximately KES 4,800 (USD 55, PPP 77) per replacement, implying a simple return on the investment in the roof of between 7 and 14%. Reported savings balances double as a result of cash transfers, but from low initial levels (PPP USD 10)." Haushofer and Shapiro 2013 Policy Brief, pgs. 16-17

• 78
  • "We therefore next quantify the returns to these investments. To this end, we conducted a separate survey of one respondent from each of 20 villages to obtain estimates for the costs of purchasing and maintaining metal and thatch roofs. The purchase of a metal roof represents an expenditure of on average USD 564, or 75 percent of the average transfer value. In addition to a store of value (roofs can be resold), a metal roof provides an investment return to households by obviating the need to replace and repair their thatched roofs, which costs on average USD 107 per year. Together, these figures imply a simple return on the investment in the roof of 23 percent (assuming no depreciation of metal roofs; this assumption is reasonable as most respondents were unable to put an upper bound on the durability of metal roofs)." Haushofer and Shapiro 2013, pg. 34
  • "Cash transfers increase the likelihood of having an iron roof by 23 percentage points relative to a control group mean of 16%. The purchase of an iron roof represents an expenditure of approximately KES 35,220 (USD 402, PPP 564), or 75% of the average transfer value. In addition to a store of value (roofs can be resold), an iron roof potentially provides an investment return to households by obviating the need to periodically replace their thatched roofs, which must be done ever 1 to 2 years, costing approximately KES 4,800 (USD 55, PPP 77) per replacement, implying a simple return on the investment in the roof of between 7 and 14%. Reported savings balances double as a result of cash transfers, but from low initial levels (PPP USD 10)." Haushofer and Shapiro 2013 Policy Brief, pgs. 16-17

• 79
  • 30%-39% ROI in YOP. "The 2010 and 2012 earnings ITT estimates in Table III represent ROIs of 30% and 39% on the per capita grant.21 The 2010 and 2012 TOT estimates represent ROIs of 36% and 49%. . . . All these ROIs are large relative to the real commercial lending rates of 10 to 30% common among medium-size firms in Uganda. They also approach the ROIs estimated from cash grants to existing microenterprises in Sri Lanka, Mexico, and Ghana (de Mel et al., 2008; McKenzie and Woodruff, 2008; Udry and Anagol, 2006)." Blattman, Fiala, and Martinez 2013, pg. 24.
  • 36% ROI in WINGS
    • After subtracting out the effects of follow-up visits by AVSI staff, we estimate that the other components of WINGS increased beneficiaries’ monthly net earnings by an average of about $4.49/month.
      • The full WINGS program (including follow-up) increased beneficiaries’ monthly net earnings by an average of $6.50. “For the average WINGS beneficiary, net cash earnings increased UGX 16,211 in the month before the survey, a 98% increase over controls. . . . In absolute terms, an increase of UGX 16,211 does not seem large (about $6.50 at market exchange rates of 2500). . . . In absolute terms, an increase of UGX 16,211 does not seem large (about $6.50 at market exchange rates of 2500).” Blattman et al 2013, pgs. 14-15.
      • Using data from phase 2 (where some villages were randomly selected to receive no follow-up visits), Blattman et al 2013 estimate that the follow-up component was responsible for about $2.01 per month of the net earnings increase. “Those assigned to any follow-up report 27% higher cash earnings, a statistically significant increase. In absolute terms the impact is small—about 5,000 UGX per month, or USD 2.01. Since cash earnings are so low in this group, however, the relative impact on the business is substantial.” Blattman et al 2013, pg. 42.
      • We therefore estimate that WINGS increased beneficiaries’ monthly net earnings by $4.49/month ($6.50-$2.01) after the effects of follow-up are subtracted out. Please note that, even after subtracting out follow-up effects, these participants still benefitted from business skills training, the requirement to create a business plan and (in some cases) business networking training in addition to the $150 grant. We are unable to disentangle the effects of these components of WINGS but would guess that the grant was responsible for most of the earnings increase.
    • From these earnings numbers we can estimate a mean monthly return on investment of about 3.0% and a mean annual return on investment of about 35.9% on the original $150 grant.
      • Our mean monthly return: $4.49/$150 = 3.0%
      • Our mean annual return: 12*$4.49/$150 = 35.9%
      • These calculations assume that the earnings increases observed after 18 months are permanent. We would guess that this assumption is accurate.
      • Assuming (unrealistically but for the sake of argument) that no services other than the grant had any effect and varying other assumptions about time horizon and discount rate, Blattman et al 2013 estimates that the average lifetime ROI on the $150 grant was between 18% and 1,577%. Blattman et al 2013, pg. 30, Table 4.

• 80

  Note that we haven't explicitly searched for other RCTs of ongoing cash transfers that discuss investment returns since December 2013.

• 81

  “We find that household per capita consumption in 2003 is 10.84 pesos higher for original treatment households, and this difference is statistically significant (first column in Table 5). This impact amounts to a 5.6 percent increase in consumption for treatment households, even 4 years after controls started receiving program benefits. While we do not have agricultural production for the 2003 survey round, we do have home-produced consumption. We also find a significant increase in home- produced consumption (significantly different from 0 at the 10 percent level), which is consistent with a sustained increase in agricultural productivity (second column in Table 5).” Gertler, Martinez and Rubio-Codina 2012, pg 179.

• 82

  “Eligible households in treatment communities began receiving benefits starting in March/April of 1998, while eligible house- holds in control communities were incorporated in November/December of 1999. In order to minimize anticipation effects, households in control communities were not informed that Oportunidades would provide benefits to them until two months before incorporation. Behrman and Todd (1999) confirm that the original randomization balanced the control and treatment communities; and Attanasio, Meghir, and Santiago (forthcoming) explicitly test, but find no evidence of, anticipation effects amongst control households.” Pgs 168-169. This implies that treatment communities received an additional 20 months of transfers relative to control communities.

  Table 8 reports that mean actual transfer per adult equivalent in treatment households in October 1998 was 24.196, in May 1999 was 38.691, and in November 1999 was 31.141. The mean of these values is 31.34. Multiplying by 20, for the number of months that the treatment communities received treatment and the control communities did not, we estimate that treatment caused an average transfer of 627 pesos per adult equivalent in the treatment group before the control group began to be treated.

  Four years later, consumption was 10.84 pesos per adult equivalent per month higher in the treatment group, implying a 1.7% (10.84/627) monthly return. 10.84/627*12 = 20.746%

• 83

  Table 8 reports that the difference between monthly transfer and increase in consumption was:

  • October 1998: 24.196 – 17.613= 6.583
  • May 1999: 38.691 – 16.033 = 22.658
  • November 1999: 31.141 – 14.596 = 16.545

  This implies a mean savings from transfers of 15.262 per month, or 305.24 over the period of treatment prior to the control group receiving treatment.

  Four years later, consumption was 10.84 pesos per adult equivalent per month higher in the treatment group, implying a 3.6% (10.84/305) monthly return and 42.6% annual return.

• 84

  Gertler, Martinez and Rubio-Codina 2012:

  • “The second coefficient, ρg. 12 , represents the effect on consumption of transfers made in the second 12-month period prior to the current transfers. This coefficient is positive and significantly different from zero. We estimate that for every peso transferred during this period, current consumption increased by 1.8 cents. The third coefficient represents the effect on consumption of transfers made in the period prior to 24 months before the current transfer period. This coefficient is positive and significantly different from zero, and implies that for every peso transferred during this period, current consumption increased by 1.6 cents. While this coefficient is slightly lower than the second lag, the two are not significantly different from one another, as reported in the sixth row of Table 10 ( p-value = 0.805). This suggests at best a slight drop off in the MIE due to depreciation.
    Using these estimates of MPC and MIE, we run a back-of-the-envelope calculation to predict the long-term effects of the cash transfers on living standards, simply multiplying the MIE by total cumulative transfers. By November 2003, after 51/2 years on the program, households in the treatment group had received a total of 2,624 pesos per capita, on average.28 Using our more conservative estimate of the MIE of 0.016, this implies an increase in consumption of 41.9 pesos per capita per month through the investment pathway. If these increases in consumption are, as argued here, derived from productive investments made by beneficiary households thanks to the cash transfers, then to the extent that the investments are long term, these increases in living standards are expected to be sustained over time even after the household is no longer receiving cash transfers from Oportunidades.” Pg 190.
  • “We estimate the MPC to be 0.74, implying that approximately three-quarters of the transfers are directly consumed and one-quarter are invested. The estimated MPC is significantly different from 1 at conventional significance levels, as the test in the fifth row in Table 6 reports ( p-value = 0.008). We also tested, and could not reject ( p-value of 0.956), the hypothesis that the MPC is the same for all four rounds of the data used (results available upon request).” Pg 189.

• 85

  19.2% per year / 26% invested = 73.8% annual return on invested funds.
  1.6% per month/ 26% invested = 6.2% monthly return on invested funds.

• 86

  Gertler, Martinez and Rubio-Codina 2012. “We solve this problem by instrumenting current transfers and past cumulative transfers with the maximum potential current and maximum potential past cumulative transfers, respectively, that a family could achieve if the maximum number of eligible children in the household were enrolled in school.27 At each time t, we compute a family’s maximum potential transfer using a modified version of the formula in (9) and assuming that all eligible children that were enrolled at baseline have advanced a grade per year. Because of the cap on total benefits and because the transfers are zero for the first three years of school, potential transfers are a nonlinear function of the number of children at baseline who could be enrolled in school in period t.
  Maximum potential transfers and the three lagged maximum potential cumulative transfers are likely to be valid instruments for three reasons. First, they are strong predictors of the actual transfers and the three actual cumulative lagged transfer variables. Indeed, and as expected, the distribution of potential transfers follows that of the actual transfers very closely, albeit potential transfers are an overestimate of the actual transfers (given noncompliance, administrative delays in payments, etc.). The simple correlation amongst both variables is 0.89. After controlling for time effects and baseline covariates, 55.7 and 65.9 percent of the variation in current and cumulative lagged transfers are explained by their potential counterparts.
  Second, they are unlikely to be correlated with consumption via other pathways, such as other income sources. Indeed, they are uncorrelated with changes in children’s labor supply due to the program as they are computed assuming that all eligible children enrolled at baseline are still in school and have advanced one school grade per school year. Nonetheless, the transfers could also be taken in leisure by reducing adult labor supply, which would reduce household income and therefore household consumption. Everything else held constant, this would imply a down- ward biased estimate of the MPC. Parker and Skoufias (2000) show that there is no effect of the program on adult labor supply, and we can thus safely assume that the transfer variables are not correlated with other earned sources of income.
  Regarding program impacts on unearned income, the crowding out effect of pri- vate transfers found in Albarran and Attanasio (2005) and discussed earlier, would suggest that our estimated MPC is underestimated. However, private transfers are unlikely to explain our results as the crowding out effects are small in size and, on average, approximately 7.3 percent of eligible households report receiving private transfers over the experimental period (fourth column in Table 6). This proportion doubles to 15.4 percent in November 2003 (see the fifth column in Table 5) suggest- ing that the crowding effects are not sustained over time.
  Finally, there is no bias from omitted family demographic structure as we directly control for family structure in the regression models. In fact, maximum potential transfers are not strongly correlated with the number of children in the household because of the nonlinear allocation rule. Let’s imagine the following extreme situations: a household with three girls in grade 2 of primary school, and a household with three girls in grade 2 of junior high school. Both households have three female children, but while the first household will receive no school transfers, the latter household will receive a large monthly transfer. In addition, families with four or more children in junior high school would receive the same transfer amount as the latter household because the cap on total benefits would be binding. Indeed, the data shows low correlations between transfers and the number of children under 17 (r = 0.14), or with the number of siblings 15–17 years old (r = 0.42), 12–14 years old (r = 0.22), 6–11 years old (r = −0.12), and 0–5 years old (r = −0.10). Thus, we are able to explicitly control for household size and the number of children in the household in the empirical specification, which allows for identification of the potential transfer variable.” Pgs 187-188.

• 87

  Gertler, Martinez and Rubio-Codina 2012. Table 10, column 2. Pg 189. This implies an 18% annual return on transfers (12*1.5%=18%) and a 35% annual return on investment (12*1.5%/(1-.487)=35.1%).

• 88

  “One potential concern with this specification is that the current and cumulative transfer amounts that the household actually receives are determined in part by whether children attend school. If a household sends their children to work instead of going to school, then the family would have lower transfers but higher income from the child’s work. This would imply a downward biased estimate of the MPC and an upward biased estimate of the MPI. In reality, this is a concern for our estimates given that Parker and Skoufias (2000) and Skoufias and Parker (2001) find that the program reduces child labor and increases enrollment in junior high (secondary) schools as the opportunity cost of these children being in the labor force is now higher. Schultz (2004) also finds positive effects for primary school and, more notably, junior high school enrollment for boys and girls.” Gertler, Martinez and Rubio-Codina 2012, pg 187.

• 89

  Gertler, Martinez and Rubio-Codina 2012, table 10, column 1.

• 90
  • de Mel, McKenzie, and Woodruff 2008.
  • de Mel, McKenzie, and Woodruff 2012

  Both papers focus on the two-thirds of the initial sample that were not directly affected by the 2004 Indian Ocean Tsunami; including those firms that were affected would increase the estimated returns. The heterogeneity across tsunami-exposed areas is described in column 6 of Table 3 and discussion on page 1347 of de Mel, McKenzie, and Woodruff 2008.

  In general, the authors selected their sample by picking regions with high-percentage of self-employed workers and low education levels. The authors describe the remainder of the selection process: "The full survey was given to 659 enterprises meeting these criteria. After reviewing the baseline survey data, we eliminated 41 enterprises either because they exceeded the 100,000 LKR maximum size or because a follow-up visit could not verify the existence of an enterprise. The remaining 618 firms constitute the baseline sample. We present results later in the paper indicating that returns to capital were higher among firms directly affected by the tsunami, but we exclude these firms for most of the analysis because the tsunami recovery process might affect returns to capital. We leave the full analysis of the impact of the capital shocks on enterprise recovery to another paper. Excluding the directly affected firms leaves us with a baseline sample of 408 enterprises. The 408 firms are almost evenly split across two broad industry categories, with 203 firms in retail sales and 205 in manufacturing/services. Firms in retail sales are typically small grocery stores. The manufacturing/services firms cover a range of common occupations of microenterprises in Sri Lanka, including sewing clothing, making lace products, making bamboo products, repairing bicycles, and making food products such as hoppers and string hoppers" (de Mel, McKenzie, and Woodruff 2008, Pgs 1334-1335)

• 91

  de Mel, McKenzie, and Woodruff 2012. “[W]e found long-lasting impacts from one-time grants given in a randomized experiment to subsistence firms. Five years after we gave $100 or $200 to 115 of 197 male and 100 of 190 female Sri Lankan microenterprise owners, we found 10-percentage-point-higher enterprise survival rates, and $8-to-$12-per-month-higher profits for male-owned businesses that received the grants. Female-owned businesses showed no long-term (or short-term) impacts. Our follow-up investigation interviewed 94% of the original sample and collected survivorship data
  from the remaining 6%, demonstrating that tracking long-term outcomes is both feasible and worthwhile.” Abstract.

• 92

  de Mel, McKenzie, and Woodruff 2012. “For males, a 10,000 LKR grant increased monthly profits by 600 to 1200 LKR, a 6 to 12% monthly real return. This persists throughout the time period and does not narrow dramatically (as would be the case with a temporary effect) or increase dramatically (as would be the case if returns compounded). This effect is robust, and strengthened, when we look at labor income and include the labor income for those businesses which have closed, and are shown in SOM text 5 to be robust to any selective attrition.” pg 965.

• 93

  de Mel, McKenzie, and Woodruff 2008. “[W]e find that the measured effect of the cash treatment is larger than the effect of the in-kind treatment (a 6.7% vs. 4.2% monthly return), but the difference is not significant at conventional levels ( p = .45). Column (5) shows that we cannot rule out linearity of the returns measured by the two treatment levels. Profits increase by 760 LKR per month with the smaller treatment, 7.6% of the treatment amount, whereas they increase by 900 LKR per month, or 4.5% of the larger treatment. The difference in returns is not significant.” pg 1347.

• 94

  de Mel, McKenzie, and Woodruff 2008. Table V.

• 95

  de Mel, McKenzie, and Woodruff 2012. Table 3.

• 96

  Fafchamps et al. 2011:

  • “The first four columns of Table 3 show the treatment effects for the pooled sample. All four specifications show a large positive impact of the in-kind treatment on firm profits. Monthly firm profits are estimated to be 31-43 cedis higher as a result of the 150 cedis in-kind treatment. The cash treatment is significant at the 10 percent level in the untrimmed OLS specification, but becomes insignificant when trimming or using fixed effects. The coefficients are always much smaller than for the in-kind treatment, and we can reject equality of cash and in-kind grants at the 5 percent significant level for three out of four specifications and at the 10 percent level for the other. That is, cash grants have less impact on business profits than in-kind grants.” Pg 23.
  • Study participants were selected from two cities in Ghana during an initial screen. The authors describe the rest of the selection process: “The gender and business sector of all individuals passing this screen were then recorded. This resulted in screening 7,567 households to identify 3,907 individuals who passed the screen. Only 19.4 percent of these individuals were male, confirming the predominance of women among small enterprise operations in urban Ghana. We classified business sector into male-dominated industries, identified as construction, repair services, manufacturing, and shoe making and repair; female-dominated industries, identified as hair and beauty care, and food and restaurant sales; and mixed industries, identified as trade and retail, and sewing and tailoring. This classification into male-dominated, female-dominated, or mixed was based on the gender mix of selfemployed in these industries in the 2000 Census. These industries cover the vast majority of the industries in which the self-employed work in Ghana. The 4.6 percent of those screened who worked in other industries such as communication services, pharmacy, photography, fishing, and agriculture were not included in the sample. Our aim was then to arrive at a sample of roughly 900 baseline firms stratified by gender and sector. In order to minimize the spillovers from the treatments to be carried out, we did not want to select too many individuals from any given EA who were in the same line of business. We therefore randomly selected up to 5 males in male-dominated and up to 5 males in mixed industries from each EA, and up to 3 females in female-dominated and up to 3 females in mixed industries from each EA to survey, in the process ensuring that only one individual was chosen from any given household. This resulted in an initial sample of 907 firms, consisting of 538 females and 369 males. A baseline survey of these firms was conducted in October and November 2008. The firm owners were asked for details of both their firm and their household.” Pgs 14-15.

• 97

  McKenzie and Woodruff 2008:

  • “The results from table 5 show the treatment effects that are significant for two-stage least squares and instrumental variables random-effects estimation and marginally significant for instrumental variables fixed-effects estimation after 5 percent trimming. The estimated treatment effect ranges from 28.8 to 45.6 percent. It is well identified only for the subset of firms without very noisy profit data that take up the treatment when assigned.” Pg 473.
  • “The initial survey was conducted in November 2005, reflecting data from October 2005. Subsequent surveys were administered quarterly, with the fifth and last survey conducted in November 2006.” Pg 460.
  • “Before the first round of the survey, firms were told that the only compen- sation that they would receive for participating was a chance of receiving either cash or capital through prizes to be given after each survey round.6 The prize was a grant of 1,500 pesos (about $140). After the first round of the survey, a single draw from a computerized random number generator was used to ran- domly assign firms to treatment and control groups.7 Among the firms assigned to treatment status, the random draw also determined the round in which they would be treated and whether they would receive their grant as cash or capital for their enterprise. The results of the initial random draw were not revealed to either the survey company or the firms in the sample. After each round, the survey company was given a list of firms to which to distribute the grants. Each firm could receive a prize at most once, although this was not made explicit to the firms.” Pg 466.

• 98

  “Estimates of the treatment effects allowing for interactions between treatment and different measures of lack of financial constraints are reported after again eliminating firms with percentage changes in profits below the 5th per- centile or above the 95th percentile. Columns 1 and 2 of table 7 show a large and strongly significant interaction effect between treatment and whether a firm owner reports that finance is not a constraint to business growth. One cannot reject the possibility that firms that report that finance is not a constraint have no increase in profits from the treatment (the point estimate actually shows a decrease in profits). The treatment effect is much stronger for the 64 percent of firms that report that finance is a constraint: monthly profits increase 1,051–1,192 pesos for these firms, a 70–79 percent return. Similar but less significant interaction effects are found for the measures of previous use of credit. One cannot reject the possibility that there is no treatment effect for firms that previously had formal loans or sup- plier credit; the treatment effect for financially constrained firms is always positive, and it is significant in all but one case (firms that have not had a formal loan).
  The different measures are combined to create a set of firms that report that finance is a constraint to business growth and that have never had a formal loan or supplier credit. The 38 percent of firms that fall into this category are referred to as “financially superconstrained.” Interacting this variable with the treatment increases the profits among these firms by 1,430–1,515 pesos—an incredible 100 percent return.” McKenzie and Woodruff 2008, Pg 479.

• 99

  McKenzie and Woodruff 2008. “One potential concern is whether the process of trimming combined with attrition could be biasing the results. Attrition rates are similar for firms assigned to the control and treatment groups. However, after 5 percent trimming, attrition after five rounds is 58 percent for the control group and 55 percent for the group assigned to treatment.” McKenzie and Woodruff 2008 Pg 476.

• 100
  • Pre-registration of studies is the #1 change GiveWell would like to see in the social sciences. See GiveWell's suggestions for the social sciences.
  • "A goal of this study was to provide a comprehensive picture of the impacts of unconditional cash transfers on households. We therefore collected a large number of outcomes and endeavor in this paper to report the full breadth of the evidence. However, ambition makes it necessary to find a way to report all relevant results without being overwhelming and without cherry-picking. To discipline our analysis of the reduced from evidence, we wrote a pre-analysis plan (PAP) for this study, which is published and time-stamped at www.socialscienceregistry.org (Casey, Glennerster, and Miguel 2012; see also Rosenthal 1979; Simes 1986; Horton and Smith 1999). In the PAP, we specify the variables to be analyzed, the construction of indices, our approach to dealing with multiple inference, the econometric specifications to be used, and the handling of attrition. The reduced form analyses and results reported in this paper correspond to those outlined in the PAP, with the exception of the restriction of the sample to thatched-roof households at endline when identifying spillover effects to account for the time delay in applying the thatched roof criterion to the pure control group. However, this restriction is conservative. The PAP did not cover the extra analysis that is described in Sections 5.1 and 5.2 (calculation of elasticities and discount rates); however, these analyses follow standard methods, and in addition their goal is not to estimate treatment effects, but to understand mechanisms." Haushofer and Shapiro 2013, Pg. 16
  • "Due to the large number of outcome variables in the present study, false positives are a potential concern when conventional approaches to statistical inference are used. We employ two strategies to avoid this problem, following broadly the approaches of Kling et al. (2007), Anderson (2008), and Casey et al. (2012).
    First, we compute standardized indices for several main groups of outcomes, and choose focal variables of interest for others (all specified in the PAP). In particular, we use the total value of household assets, total household consumption in the past month, and total household agricultural and business income in the past month, as focal variables for the asset, consumption, and income outcome groups, respectively. For psychological well-being, food security, female empowerment, health, and education, we compute indices, which are standardized weighted averages of several key outcomes of interest within each of these groups of outcomes. The particular outcomes composing each index and the focal variables were pre-specified in our pre-analysis plan.
    Second, even after collapsing variables into indices and choosing focal variables of interest for each group of outcomes, we are still left with multiple indices, creating the need to further control the probability of Type I errors. To this end, we use the Family-Wise Error Rate (FWER; Westfall, Young, and Wright 1993; Efron and Tibshirani 1993; Anderson 2008; Casey, Glennerster, and Miguel 2012), which controls the probability of Type I errors across a group of coefficients. In our case, we control the FWER across the treatment coefficients on the indices for our main outcome groups, i.e. assets, consumption, income, psychological well-being, education, food security, health, and female empowerment. As specified in our pre-analysis plan, we apply this correction to the index variables only; when discussing individual variable results within particular outcome groups, we use conventional significance levels. We use this approach because the purpose of studying indi- vidual variables within the outcome groups is to understand mechanisms, rather than to single out particular variables for general conclusions." Haushofer and Shapiro 2013, Pgs. 18-19

• 101

  “Large vs. small transfers Finally, a third treatment arm was created to study the relative impact of large compared to small transfers. To this end, 137 households in the treatment group were randomly chosen and informed in January 2012 that they would receive an additional transfer of KES 70,000 (USD 798, PPP 1,112), paid in seven monthly installments of KES 10,000 (USD 114, PPP 160) each, beginning in February 2012. Thus, the transfers previously assigned to these households, whether monthly or lump-sum, were augmented by

  KES 10,000 from February 2012 to August 20128, and therefore the total transfer amount received by these households was KES 95,200 (USD 1,085, PPP 1,525). The remaining 348 treatment households constitute the “small” transfer group, and received transfers totaling KES 25,200 (USD 287, PPP 404) per household.

  These three treatment arms were fully cross-randomized, except that, as noted above, the “large” transfers were made to existing recipients of KES 25,200 transfers in the form of a KES 70,000 top-up that was delivered as a stream of payments after respondents had already been told that they would receive KES 25,200 transfers. Section 3.1 outlines how this issue is dealt with in the analysis.” Haushofer and Shapiro 2013 Policy Brief, pgs. 7-8.

• 102
  • “We conducted a randomized controlled trial (RCT) of the unconditional cash transfer program implemented by the NGO GiveDirectly in Western Kenya between 2011 and 2012, in which poor rural households received unconditional cash transfers through the mobile money system M-Pesa.” Haushofer and Shapiro 2013 Policy Brief, pg. 1.
  • GiveDirectly recently expanded into Uganda. See our review of GiveDirectly.

• 103
  • See our review of GiveDirectly for more information on GiveDirectly's standard model.
  • “[GiveDirectly] selects poor households by first identifying poor regions of Kenya according to census data. In the case of the present study, the region chosen was Rarieda, a peninsula in Lake Victoria west of Kisumu in Western Kenya. Following the choice of a region in which to operate, GD identifies target villages. In the case of Rarieda, this was achieved through a rough estimation of the population of villages and the proportion of households lacking a solid roof; villages with a high proportion of households living in thatched roof homes (rather than iron), which is GD’s targeting criterion, were prioritized. The criterion was established by GD in prior work as an objective and highly predictive indicator of poverty.” Haushofer and Shapiro 2013 Policy Brief, pg. 4.

• 104

  “This study employs a two-level cluster-randomized controlled trial. An overview of the design is shown in Figure 1. In collaboration with GD, we identified 126 villages from a list of villages in Rarieda district of Western Kenya. In the first stage of randomization, 63 of these villages were randomly chosen to be treatment villages. Within all villages, we conducted a census with the support of the village elder, which identified all eligible households within the village. As described above, eligibility was based on living in a house with a thatch roof. Control villages were only surveyed at endline; in these villages, we sampled 432 households from among eligible households, to which we refer as “pure control” households in the following.

  In treatment villages, we performed a second stage of randomization, in which we randomly assigned 50% of the eligible households in each treatment village to the treatment condition, and 50% to the control condition. This process resulted in 503 treatment households at baseline, and 505 control households in treatment villages, to which we refer as “spillover” households in the following.” Haushofer and Shapiro 2013 Policy Brief, pg. 6.

• 105

  “We therefore focus on the within-village treatment effect when reporting results; in the presence of positive spillovers, this is a conservative estimate of the treatment effect.6 Footnote 6 states:

  “Note that this strategy would overestimate the treatment effect in the presence of negative spillovers. However, we find little evidence for negative spillovers, as discussed below; this includes psychological well-being, i.e. untreated households in treatment villages did not experience a decrease in psychological well-being. We thus believe that the within-village treatment effects are a conservative estimate.” Haushofer and Shapiro 2013 Policy Brief, pg. 6.

• 106

  “Control villages were only surveyed at endline; in these villages, we sampled 432 households from among eligible households, to which we refer as “pure control” households in the following. . . . To obtain a lower-bound estimate for spillover effects, we compare households which still have thatched roofs at endline to pure control households which still have thatched roofs at endline. The logic behind this choice is the following. First, note that in the absence of spillover effects on roof purchases, this comparison provides an unbiased estimate of the spillover effects for this group of households. Second, relax the assumption of no spillovers and assume instead (as is likely) that spillover effects predominantly induce the better-off control households in treatment villages to upgrade to an iron roof. If this is the case, restricting the sample to households which still have a thatched roof at endline selects for poorer households in treatment villages, but not pure control villages, and thus provides a lower bound estimate of the spillover effect. To be conservative, in what follows we report this lower-bound estimate.” Haushofer and Shapiro 2013 Policy Brief, pgs. 6-7.

• 107

  “A goal of this study was to assess the relative welfare impacts of three design features of unconditional cash transfers: the gender of the transfer recipient; the temporal structure of the transfers (monthly vs. lump-sum transfers); and the magnitude of the transfer. The intervention was therefore structured as follows:

  1. Transfers to the woman vs. the man in the household. Among households with both a primary female and primary male member, we stratified on recipient gender and randomly assigned the woman or the man to be the transfer recipient in an equal number of households. A further 110 households had a single household head and were therefore not considered in the randomization of recipient gender.

  2. Lump-sum transfers vs. monthly installments. Across all treatment households, we randomly assigned the transfer to be delivered either as a lump-sum amount, or as a series of nine monthly installments. Specifically, 244 of the 503 treatment households were assigned to the monthly condition, and 256 to the lump-sum condition. The total amount of each type of transfer was KES 25,200 (USD 287, PPP 404). This amount includes an initial transfer of KES 1,200 (USD 14, PPP 19) to incentivize M-Pesa registration, followed by either a lump- sum payment of KES 24,000 (USD 274, PPP 384) in the lump-sum condition, or a sequence of nine monthly transfers of KES 2,800 (USD 32, PPP 45) in the monthly condition. The timing of transfers was structured as follows: in the monthly condition, recipients received the first transfer of KES 2,800 on the first of the month following M-Pesa registration, and the remaining eight transfers of KES 2,800 on the first of the eight following months. In the lump-sum condition, recipients received an initial transfer of KSH 1,200 on the first of the month following M-Pesa registration to incentivize registration, and the lump-sum transfer of KES 24,000 on the first of a month that was chosen randomly among the nine months following the time at which they were enrolled in the GD program. This procedure ensured that the monthly and lump-sum transfers had the same net present value.

  3. Large vs. small transfers. Finally, a third treatment arm was created to study the relative impact of large compared to small transfers. To this end, 137 households in the treatment group were randomly chosen and informed in January 2012 that they would receive an ad- ditional transfer of KES 70,000 (USD 798, PPP 1,112), paid in seven monthly installments of KES 10,000 (USD 114, PPP 160) each, beginning in February 2012. Thus, the transfers previously assigned to these households, whether monthly or lump-sum, were augmented by KES 10,000 from February 2012 to August 20128, and therefore the total transfer amount received by these households was KES 95,200 (USD 1,085, PPP 1,525). The remaining 348 treatment households constitute the “small” transfer group, and received transfers totaling KES 25,200 (USD 287, PPP 404) per household.

  These three treatment arms were fully cross-randomized, except that, as noted above, the “large” transfers were made to existing recipients of KES 25,200 transfers in the form of a KES 70,000 top-up that was delivered as a stream of payments after respondents had already been told that they would receive KES 25,200 transfers. Section 3.1 outlines how this issue is dealt with in the analysis.” Haushofer and Shapiro 2013 Policy Brief, pgs. 7-8.

• 108

  We stress, however, that the current study was not designed to investigate long-term effects; further endline surveys will be required to obtain a more complete understanding of long term impacts." Haushofer and Shapiro 2013 Policy Brief, pg. 15.

• 109
  • “Endline surveys took place with September and December 31, 2012. Transfers were made between June 2011 and January 2013.” Haushofer and Shapiro 2013 Policy Brief, pg. 8.
  • The minimum, mean, and maximum time between receipt of last transfer and taking the end-line survey were 1 month, 4.7 months, and 15 months. Johannes Haushofer, co-author of GiveDirectly RCT, email to GiveWell, November 4, 2013.

• 110

  72% = 348/(137+348). "Large vs. small transfers Finally, a third treatment arm was created to study the relative impact of large compared to small transfers. To this end, 137 households in the treatment group were randomly chosen and informed in January 2012 that they would receive an additional transfer of KES 70,000 (USD 798, PPP 1,112), paid in seven monthly installments of KES 10,000 (USD 114, PPP 160) each, beginning in February 2012. Thus, the transfers previously assigned to these households, whether monthly or lump-sum, were augmented by KES 10,000 from February 2012 to August 20128, and therefore the total transfer amount received by these households was KES 95,200 (USD 1,085, PPP 1,525). The remaining 348 treatment households constitute the 'small' transfer group, and received transfers totaling KES 25,200 (USD 287, PPP 404) per household. These three treatment arms were fully cross-randomized, except that, as noted above, the 'large' transfers were made to existing recipients of KES 25,200 transfers in the form of a KES 70,000 top-up that was delivered as a stream of payments after respondents had already been told that they would receive KES 25,200 transfers. Section 3.1 outlines how this issue is dealt with in the analysis." Haushofer and Shapiro 2013 Policy Brief, Pgs. 7-8

• 111

  GiveDirectly's Grant structure

• 112
  • The PPP adjusted values of the small, mean, and large transfer are $404, $721, and $1,525 respectively. “28% of the treatment group received a transfer of KES 95,200 (USD 1,085, PPP 1,525), while the remaining 72% received KES 25,200 (USD 287, PPP 404); the average transfer was thus KES 45,016 (USD 513, PPP 721).” Haushofer and Shapiro 2013 Policy Brief, pg. 12.
  • "All USD values are calculated at purchasing power parity, using is the 2012 World Bank PPP estimate for private consumption in Kenya: 0.016." Haushofer and Shapiro 2013, Pg. 2

• 113

  Table 28, Haushofer and Shapiro 2013 Appendix, Pg. 54

• 114
  • Non-land assets includes “the value, in USD PPP, of all moveable assets the household owns, including savings, plus the value of the roof of the home.” Haushofer and Shapiro 2013 Policy Brief, pg. 10.
  • Haushofer and Shapiro 2013 Appendix, Pgs. 1-2

• 115

  Small transfers: $210 (95% CI: $158 to $263). Table 28, Haushofer and Shapiro 2013 Appendix, Pg. 54

• 116
  • Small transfers, livestock: $68 (95% CI: $35 to $100)
  • Small transfers, durable goods: $36 (95% CI: $18 to $54)
  • Small transfers, savings: $7 (95% CI: $2 to $13)
  • Table 32, Haushofer and Shapiro 2013 Appendix, Pg. 58

• 117

  Table 5, Haushofer and Shapiro 2013, Pg. 53

• 118

  Table 5, Haushofer and Shapiro 2013, Pg. 53

• 119

  "To this end, we conducted a separate survey of one respondent from each of 20 villages to obtain estimates for the costs of purchasing and maintaining metal and thatch roofs. The purchase of a metal roof represents an expenditure of on average USD 564, or 75 percent of the average transfer value." Haushofer and Shapiro 2013, Pg. 34

• 120

  "Based on the anonymized individual-level survey data, an iron roof costs $418 on average, thatch roof replacement (including the cost of grass for making the roof and the labor) costs $95 on average, and thatch roof repair (including the cost of grass for making the roof and the labor) costs $107 on average. These numbers appear to conflict with the full paper and the policy brief. It may be that the results were from a different survey. Haushofer and Shapiro have not yet finished verifying which data were used." GiveWell's non-verbatim summary of a conversation with Carolina Toth, GiveDirectly, October 1, 2014

• 121

  Table 44, Haushofer and Shapiro 2013 Appendix, Pg. 70

• 122

  Table 44, Haushofer and Shapiro 2013 Appendix, Pg. 70

• 123

  Table 36, Haushofer and Shapiro 2013 Appendix, Pg. 62

• 124

  Table 36, Haushofer and Shapiro 2013 Appendix, Pg. 62

• 125

  Table 36, Haushofer and Shapiro 2013 Appendix, Pg. 62

• 126

  Table 52, Haushofer and Shapiro 2013 Appendix, Pg. 78

• 127
  • N = 1372. Table 36, Haushofer and Shapiro 2013 Appendix, Pg. 62
  • N = 1174. Table 52, Haushofer and Shapiro 2013 Appendix, Pg. 78

• 128

  Small transfers: $31 (95% CI: $18 to $43). Table 28, Haushofer and Shapiro 2013 Appendix, Pg. 54

• 129
  • Large transfers: $25 (95% CI: $11 to $39). $25/$51 = about 50%
  • Small transfers: $18 (95% CI: $9 to $27). $18/$31 = about 60%
  • Table 36, Haushofer and Shapiro 2013 Appendix, Pg. 62

• 130
  • Large transfers, social: $3 (95% CI: $1 to $5)
  • Small transfers, social: $2 (95% CI: $1 to $3)
  • Large transfers, other: $19 (95% CI: $13 to $24)
  • Small transfers, other: $7 (95% CI: $3 to $11)
  • Table 36, Haushofer and Shapiro 2013 Appendix, Pg. 62

• 131
  • Large transfers, alcohol: -$2.07 (95% CI: -$4.6 to $0.5)
  • Small transfers, alcohol: -$0.51 (95% CI: -$2.7 to $1.7)
  • Large transfers, tobacco: -$0.38 (95% CI: -$1.0 to $0.2)
  • Small transfers, tobacco: -$0.08 (95% CI: -$0.6 to $0.4)
  • Table 36, Haushofer and Shapiro 2013 Appendix, Pg. 62

• 132

  “Food security is low in this population. Though instance of skipped meals are not extreme, 20% of the control group reports that not all household members usually eat until they are content, 23% of respondents report sleeping hungry in the last week, and only 36% report having enough food in the house for the next day.” Haushofer and Shapiro 2013 Policy Brief, pg. 18.

• 133

  Small transfers: 0.21 (95% CI: 0.07 to 0.35). Table 28, Haushofer and Shapiro 2013 Appendix, Pg. 54

• 134
  • Large transfers, health index: -0.09 (95% CI: -0.27 to 0.09)
  • Small transfers, health index: -0.02 (95% CI: -0.16 to 0.12)
  • Large transfers, education index: 0.11 (95% CI: -0.05 to 0.27)
  • Small transfers, education index: 0.07 (95% CI: -0.07 to 0.21)
  • Table 28, Haushofer and Shapiro 2013 Appendix, Pg. 54

• 135
  • Large transfers, profits: -$1 (-$10 to $8)
  • Small transfers, profits: $0.26 (-$8 to $9)
  • Table 44, Haushofer and Shapiro 2013 Appendix, Pg. 70

• 136

  Small transfers: 0.11 (95% CI: -0.01 to .23). Table 28, Haushofer and Shapiro 2013 Appendix, Pg. 54

• 137
  • Table 56, Haushofer and Shapiro 2013 Appendix, Pg. 82
  • Table 7, Haushofer and Shapiro 2013, Pg. 55

• 138
  • "These are generally small and not significant, with one exception: we observe an increase of 0.23 SD in the female empowerment index among the control group in treatment villages. This increase is significant at the 5 percent level using conventional p-values. Together with a non-significant direct treatment effect of SD −0.01 on this measure, this spillover effect suggests that the treatment group shows a significant increase in female empowerment relative to the pure control group, which we confirm in the Online Appendix. However, since this is the only outcome that shows any spillover effect and we do not have a good theory for why spillover effects might occur in female empowerment, we do not offer an interpretation of this result at this stage, and instead note that it needs to be replicated." Haushofer and Shapiro 2013, Pg. 23
  • Table 1, Haushofer and Shapiro 2013, Pg. 49

• 139

  “As changes in domestic violence were hypothesized to arise through mechanisms directly associated with cash transfers (such as a change in women’s bargaining power, or a reduction in domestic tension over economic hardships), these spillover effects are somewhat surprising. One possible explanation is that the results are simply an artifact of reporting bias, where the spillover sample believed that a different answer was desired from them than the control group. However, given that we do not find spillover effects in other measures that target unobservable outcomes, we find this explanation implausible. Another possibility is that the presence of the cash transfer program in the village motivated the husbands in untreated households to change their behavior in the hope of receiving transfers in the future. For instance, knowing that the primary female in the household was equally likely to receive the transfer as the primary male, men may have shifted their behavior to establish better relationships with their spouse. Alternatively, the spillover effect may operate through changes in attitudes among either or both husbands and wives in non-treated households. Our data does not distinguish between these possibilities; we find these unexpected results intriguing and believe they warrant further investigation.” Haushofer and Shapiro 2013 Policy Brief, pg. 21.

• 140

  "Column (3) in Table 1 reports the coefficients on the spillover dummies. These are generally small and not significant, with one exception: we observe an increase of 0.23 SD in the female empowerment index among the control group in treatment villages. This increase is significant at the 5 percent level using conventional p-values. Together with a non-significant direct treatment effect of SD −0.01 on this measure, this spillover effect suggests that the treatment group shows a significant increase in female empowerment relative to the pure control group, which we confirm in the Online Appendix. However, since this is the only outcome that shows any spillover effect and we do not have a good theory for why spillover effects might occur in female empowerment, we do not offer an interpretation of this result at this stage, and instead note that it needs to be replicated." Haushofer and Shapiro 2013, Pg. 23
  

• 141

  Point estimates suggest that the program reduced the value of nonrecipients’ non-land assets by about $19, reduced their consumption by $8 per month, and reduced their total revenues by $5 per month, but these estimates are not statistically significant. Haushofer and Shapiro 2013 Policy Brief, pg. 29.

• 142
  • ”There are no significant village-level effects on any variable group, suggesting that cash transfers to a group of particularly disadvantaged households within these villages did not impact the general village-level economy.” Haushofer and Shapiro 2013 Policy Brief, pg. 22.
  • Standard errors on these estimates appear relatively large. Haushofer and Shapiro 2013 Policy Brief, pg. 38. However, the study does not include a complete description of how these indices were constructed so we are unsure of whether these estimates include the possibility of meaningful village-level economic effects.

• 143

  “Column (4) in Table 1 reports the coefficients and standard errors comparing female to male re- cipient households on the index variables. With the exception of psychological well-being, which is significant at the 10% level, none of the differences between the treatment effects for transfers to the female vs. the male are statistically significant at conventional significance levels. Thus we find little evidence that providing cash transfers to women vs. men differentially affect outcomes. However, we note a trend in the point estimates suggesting that transferring cash to the primary male in the household leads to a larger impact on standard measures of economic welfare, namely assets and consumption, while transferring cash to the primary female in the household improves outcomes most likely to benefit children, i.e. food security, health, and education, as well as psychological well-being and female empowerment. Haushofer and Shapiro 2013 Policy Brief, pg. 13.

• 144

  “Results are shown in column (5) of Table 1. The joint significance across outcomes is at p 0.05, suggesting that monthly and lump-sum transfers have significantly different effects on our outcomes. In the individual variables, we find that monthly payments increase food security by 0.26 SD relative to lump-sum payments, which is statistically different from zero, and some indication that lump sum transfers lead to higher asset values.” Haushofer and Shapiro 2013 Policy Brief, pg. 14.

• 145

  Among households receiving small transfers, some households received their last transfer less than a month before the end-line survey while others received their final transfers more than four months before being surveyed. Haushofer and Shapiro 2013 use this variation to attempt to determine whether effects of transfers fade out immediately after the transfers end. They find:

  • moderate evidence suggesting that the impact on asset values was maintained more than four months after the final transfer;
  • moderate evidence suggesting that the impact on consumption may have declined for households receiving monthly installments but not for households that received lump-sum transfers (which spent less on consumption in the first place);
  • no evidence of changing impacts on revenues over time;
  • moderate evidence suggesting that the impact on food security for households receiving monthly installments declines over time (but remains distinguishable from zero).

  “The figure indicates that the observed average impact on overall asset values in treatment households persists over time: both for households receiving lump-sum and monthly transfers, levels of asset holdings are significantly higher than in the control group at all time horizons. We observe no decrease over time in either group; the 95% confidence intervals of the coefficients overlap across all time horizons.

  Similarly, consumption is elevated relative to control at all time horizons. The point estimates suggest declining impacts on total non-durable consumption over time for the group receiving monthly transfers, though not for the lump sum group; however, the confidence intervals of the treatment effects at shorter vs. longer time horizons overlap, i.e. these differences are not statistically significant.

  For agricultural and business revenue, we find no strong indication of changing impacts over time; however, note that the treatment effects are small overall and not distinguishable from zero in this restricted and highly disaggregated sample.

  Cash transfers also had persistent impacts on food security. However, this effect is driven by the monthly transfer group; in the lump-sum group we find little evidence of treatment effects at any time horizon, consistent with the larger overall treatment effect on food security in the monthly group. We also observe that the impact on food security is largest among the group receiving contemporaneous transfers; the treatment effect on food security falls by more than 50% over time in the group receiving monthly transfers, although remains positive and statistically different from zero.

  The temporal dynamics of cash transfers for additional outcomes (psychological well being, health, education, female empowerment) reveal no differential impacts at different delays. In the case of psychological well-being, this reflects the fact that the restricted sample used here is underpowered to detect the overall treatment effect we observe for this outcome measure.” Haushofer and Shapiro 2013 Policy Brief, p. 16. This analysis has extremely low power and includes only households receiving small transfers, so we do not have high confidence in the results.

• 146

  “Lump-sum transfers vs. monthly installments. Across all treatment households, we randomly assigned the transfer to be delivered either as a lump-sum amount, or as a series of nine monthly installments. Specifically, 244 of the 503 treatment households were assigned to the monthly condition, and 256 to the lump-sum condition. The total amount of each type of transfer was KES 25,200 (USD 287, PPP 4047). This amount includes an initial transfer of KES 1,200 (USD 14, PPP 19) to incentivize M-Pesa registration, followed by either a lump- sum payment of KES 24,000 (USD 274, PPP 384) in the lump-sum condition, or a sequence of nine monthly transfers of KES 2,800 (USD 32, PPP 45) in the monthly condition. The timing of transfers was structured as follows: in the monthly condition, recipients received the first transfer of KES 2,800 on the first of the month following M-Pesa registration, and the remaining eight transfers of KES 2,800 on the first of the eight following months. In the lump-sum condition, recipients received an initial transfer of KSH 1,200 on the first of the month following M-Pesa registration to incentivize registration, and the lump-sum transfer of KES 24,000 on the first of a month that was chosen randomly among the nine months following the time at which they were enrolled in the GD program. This procedure ensured that the monthly and lump-sum transfers had the same net present value.” Haushofer and Shapiro 2013 Policy Brief, p. 7. Households that received lump sums in early months therefore received their final transfers much earlier than other households.

• 147
  • For example, the survey’s questions about non-agriculture flow expenses, non-agricultural business investment in durables, farm revenue, and farm flow expenses are backwards looking and are therefore cover periods of time when more households had not received their full transfers.
  • ”In the last 12 months what was spent on machinery or durable goods (e.g., tools, cooking pots, overs, sewing machines)?” GiveDirectly Survey for Randomized Controlled Trial.
  • ”In the last 3 months what was spent for this enterprise on:
    • Electricity
    • Salaries/wages
    • Water
    • Transport
    • Purchase of inputs, inventory, and products
    • Other costs (exclude machinery, tools, durables already mentioned in V84)”

    GiveDirectly Survey for Randomized Controlled Trial.

  • ”[During the long/short rain season] How much did your household receive for the amount it sold?”
  • ”In the last long[/short] rains season how much did your household pay for:
    • Seeds
    • Fertilizers/pesticides/herbicides
    • Hiring Machines (e.g. for plowing or spraying)
    • Water (including irrigation water)
    • Hiring Labor
    • Other expenses

    GiveDirectly Survey for Randomized Controlled Trial.

• 148

  "In particular, we find increases in holdings of home durables (notably metal roofs, ownership of which increased by 23 percentage points over a control group mean of 16 percent), and productive assets such as livestock, whose value increases by USD 85 over a control group mean of USD 167." Haushofer and Shapiro 2013, Pg. 3
  

• 149

  Annual investment return = $107/$564 = 19%. Haushofer and Shapiro also report an internal rate of return (IRR), or the annual discount rate such that the net present value of the investment returns equal the cost of the investment (i.e. the sum of $107/(1 + IRR)^t from t = 0 to t = Infinity equals $564), of 23%. "We therefore next quantify the returns to these investments. To this end, we conducted a separate survey of one respondent from each of 20 villages to obtain estimates for the costs of purchasing and maintaining metal and thatch roofs. The purchase of a metal roof represents an expenditure of on average USD 564, or 75 percent of the average transfer value. In addition to a store of value (roofs can be resold), a metal roof provides an investment return to households by obviating the need to replace and repair their thatched roofs, which costs on average USD 107 per year. Together, these figures imply a simple return on the investment in the roof of 23 percent (assuming no depreciation of metal roofs; this assumption is reasonable as most respondents were unable to put an upper bound on the durability of metal roofs)." Haushofer and Shapiro 2013, pg. 34

• 150

  "To this end, we conducted a separate survey of one respondent from each of 20 villages to obtain estimates for the costs of purchasing and maintaining metal and thatch roofs." Haushofer and Shapiro 2013, pg. 34

• 151

  "GiveDirectly conducted a survey of 20 random CT recipients from 20 different villages. The sampling method entailed calling one person at random in each of the randomly selected villages until someone answered the phone and was able to provide answers to the survey questions." GiveWell's non-verbatim summary of a conversation with Carolina Toth, GiveDirectly, October 1, 2014

• 152
  • ($95+$107)/$418 = 0.48. "Based on the anonymized individual-level survey data, an iron roof costs $418 on average, thatch roof replacement (including the cost of grass for making the roof and the labor) costs $95 on average, and thatch roof repair (including the cost of grass for making the roof and the labor) costs $107 on average. These numbers appear to conflict with the full paper and the policy brief. It may be that the results were from a different survey. Haushofer and Shapiro have not yet finished verifying which data were used." GiveWell's non-verbatim summary of a conversation with Carolina Toth, GiveDirectly, October 1, 2014
  • Note that the cost the survey found for thatch roof repair was the same as the repair and replacement costs in Haushofer and Shapiro 2013: "The purchase of a metal roof represents an expenditure of on average USD 564, or 75 percent of the average transfer value. In addition to a store of value (roofs can be resold), a metal roof provides an investment return to households by obviating the need to replace and repair their thatched roofs, which costs on average USD 107 per year." Haushofer and Shapiro 2013, pg. 34

• 153

  Haushofer and Shapiro 2013 Policy Brief estimated an annual investment return of 7% (($77/2)/$564) or 14% ($77/$564): "Cash transfers increase the likelihood of having an iron roof by 23 percentage points relative to a control group mean of 16%. The purchase of an iron roof represents an expenditure of approximately KES 35,220 (USD 402, PPP 564), or 75% of the average transfer value. In addition to a store of value (roofs can be resold), an iron roof potentially provides an investment return to households by obviating the need to periodically replace their thatched roofs, which must be done ever 1 to 2 years, costing approximately KES 4,800 (USD 55, PPP 77) per replacement, implying a simple return on the investment in the roof of between 7 and 14%. Reported savings balances double as a result of cash transfers, but from low initial levels (PPP USD 10)." Haushofer and Shapiro 2013 Policy Brief, pgs. 16-17

• 154
  • "We therefore next quantify the returns to these investments. To this end, we conducted a separate survey of one respondent from each of 20 villages to obtain estimates for the costs of purchasing and maintaining metal and thatch roofs. The purchase of a metal roof represents an expenditure of on average USD 564, or 75 percent of the average transfer value. In addition to a store of value (roofs can be resold), a metal roof provides an investment return to households by obviating the need to replace and repair their thatched roofs, which costs on average USD 107 per year. Together, these figures imply a simple return on the investment in the roof of 23 percent (assuming no depreciation of metal roofs; this assumption is reasonable as most respondents were unable to put an upper bound on the durability of metal roofs)." Haushofer and Shapiro 2013, pg. 34
  • "Cash transfers increase the likelihood of having an iron roof by 23 percentage points relative to a control group mean of 16%. The purchase of an iron roof represents an expenditure of approximately KES 35,220 (USD 402, PPP 564), or 75% of the average transfer value. In addition to a store of value (roofs can be resold), an iron roof potentially provides an investment return to households by obviating the need to periodically replace their thatched roofs, which must be done ever 1 to 2 years, costing approximately KES 4,800 (USD 55, PPP 77) per replacement, implying a simple return on the investment in the roof of between 7 and 14%. Reported savings balances double as a result of cash transfers, but from low initial levels (PPP USD 10)." Haushofer and Shapiro 2013 Policy Brief, pgs. 16-17

• 155
  • Haushofer and Shapiro 2013 Policy Brief, p. 25.
  • ”A goal of this study was to assess the relative welfare impacts of three design features of unconditional cash transfers: the gender of the transfer recipient; the temporal structure of the transfers (monthly vs. lump-sum transfers); and the magnitude of the transfer.” Haushofer and Shapiro 2013 Policy Brief, p. 7.

• 156

  “We therefore focus on the within-village treatment effect when reporting results; in the presence of positive spillovers, this is a conservative estimate of the treatment effect.” Haushofer and Shapiro 2013 Policy Brief, p. 6.

• 157

  “We therefore focus on the within-village treatment effect when reporting results; in the presence of positive spillovers, this is a conservative estimate of the treatment effect.6” Footnote six says: “Note that this strategy would overestimate the treatment effect in the presence of negative spillovers. However, we find little evidence for negative spillovers, as discussed below; this includes psychological well-being, i.e. untreated households in treatment villages did not experience a decrease in psychological well-being. We thus believe that the within-village treatment effects are a conservative estimate.” Haushofer and Shapiro 2013 Policy Brief, p. 6.

• 158
  • “Recipients increased asset holdings by PPP USD 279.” Haushofer and Shapiro 2013 Policy Brief, pg. 2.
  • ”Similarly, the transfers increase the treatment group’s average monthly consumption by PPP USD 36 at endline, which corresponds to 23% of average consumption among control households.” Haushofer and Shapiro 2013 Policy Brief, pg. 12.

• 159

  “Recipient households also report PPP USD 2 higher income from the sale of livestock and meat than control households. These effects translate into an overall increase in monthly revenues for recipient households, PPP USD 15 higher (including revenues from the sale of animals and meat), but we do not observe a significant increase in estimated profits from self-employment.” Haushofer and Shapiro 2013, p. 6.

• 160

  “YOP invited groups of young adults, aged roughly 16 to 35, to apply for cash grants in order to start a skilled trade such as carpentry or tailoring. . . . Groups in our sample ranged from 10 to 40 people, averaging 22, mostly from the same village. Half the groups existed already, often for several years, as farm cooperatives, or sports, drama, or microfinance clubs. New groups formed specifically for YOP were often initiated by a respected community member (e.g. teachers, local leaders, or existing tradespersons) and sought members through social networks. In our sample, 5% of groups are all female and 12% are all male, but most groups are mixed—about one-third female on average.” Blattman, Fiala, and Martinez 2013, pgs. 6-7.

• 161

  “From Table II, we see that members of the 535 eligible groups were generally young, rural, poor, credit constrained, and underemployed. In 2008 they were 25 years on average, mainly aged 16 to 35. Less than a quarter lived in a town, and most lived in villages of 100 to 2000 households. A quarter did not finish primary school, but on average they reached eighth grade.

  In 2008 the sample report 11 hours of work a week. Half these hours are a mix of low-skill labor or petty business, while the other half is in agriculture—a mix of subsistence and rudimentary cash crop production on small rain-fed plots with little equipment or inputs. Almost half of our sample reports no employment in the past month, and only 6% are engaged in a skilled trade. Cash earnings in the past month average roughly a dollar a day. Savings are roughly $15 on average. Only 11% report any savings, and these report $58 at the median. 33% hold loans, but these are small: under $7 at the median among those who have any loans, mainly from friends and family. About 10% report they could obtain a large loan of 1,000,000 UGX (about $580). Although poor by any measure, these applicants are slightly wealthier and more educated than their peers. If we compare our sample to people of the same gender, age and district in a 2008 population-based household survey by the government, our sample has 1.7 years more education, 0.15 SD more wealth, is 7.5 pp more urban and 5.4 pp more likely to be married, and has 1.6 fewer household members (See Appendix B.3). Given that the three most war-affected districts did not participate in the YOP evaluation, and only 3% were involved in an armed group in any fashion.” Blattman, Fiala, and Martinez 2013, pg. 11.

• 162
  • Facilitators helped the groups prepare the proposals. ”Many applicants were functionally illiterate and so YOP also required “facilitators”—usually a local government employee, teacher, or community leader—to meet with the group several times, advise them on program rules, and help prepare the written proposals. Groups chose their own facilitators, and facilitators received 2% of funded proposals (up to $200).” Blattman, Fiala, and Martinez 2013, pg. 7.
  • “Second, groups had to submit a written proposal stating how they would use the grant for non-agricultural skills training and enterprise start-up costs. They could request up to $10,000.” Blattman, Fiala, and Martinez 2013, pg. 7.

• 163

  “Finally, successful proposals received a large lump sum cash transfer to a bank account in the names of the management committee, with no government monitoring thereafter.” Blattman, Fiala, and Martinez 2013, pg. 8.

• 164

  “Per capita grant size varied across groups due to variation in group size and amounts requested. 80% of grants were between $200 and $600 per capita, averaging $382.“ Blattman, Fiala, and Martinez 2013, pg. 8.

• 165

  “Most groups proposed a single trade for all, but a third of groups proposed that different members would train two to three different trades. Females and mixed groups often chose trades common to both genders, such as tailoring or hairstyling. Males and a small number of females often chose trades such as carpentry or welding.” Blattman, Fiala, and Martinez 2013, pg. 7.

• 166
  • “At the median, they estimate they spent 11% on skills training, 52% on tools, 13% on materials, and 24% was shared in cash or spent on other things.” Blattman, Fiala, and Martinez 2013, pg. 17.
  • Training generally consisted of apprenticeships with artisans or small institutes. “In preparing the proposal, groups selected their own trainers, typically a local artisan or small institute. These are commonplace in Uganda (as in much of Africa) and there is a tradition of artisans taking on paying students as apprentices. Most of these artisans and institutes had been in existence more than five years, and most took students previously. In our sample, few were located in the village but the median artisan or institute was within 8km. Groups would travel to be closer to trainers, or paid transport and upkeep for trainers to come to them. Thus groups were seldom constrained in their choice of vocation by local trainers. This group-based training generally produced bulk discounts, and enabled a wider choice of vocations.” Blattman, Fiala, and Martinez 2013, pg. 7.

• 167
  • “Between 2008 and 2010, 68% percent of the treatment group enrolled in vocational training, compared to 15% of the control group.14 On average, treatment translates into 340 more hours of vocational training than controls.” Blattman, Fiala, and Martinez 2013, pg. 17-18.
  • “Among those who enroll in any training, 38% train in tailoring, 23% in carpentry, 13% in metalwork, 8% in hairstyling, and the remainder in miscellaneous other trades.” Blattman, Fiala, and Martinez 2013, pg. 18.

• 168

  “Treatment also increases capital stocks. We calculate the respondent’s estimated total value of all business assets and deflate it to 2008 UGX. From Table III, the control group reports UGX 290,200 ($167) of business assets in 2010 and 392,800 ($228) in 2012. By 2010 treatment increases capital stocks by UGX 377,023 ($219), a 131% increase over the control group, and by 2012 stocks increase by UGX 224,986 ($130), a 57% increase over the control group. The relative impact falls over time as the control group’s investment begins to catch up, rising 38% between 2010 and 2012 (Table IV). The bulk of this investment is in petty business and agriculture.” Blattman, Fiala, and Martinez 2013, pg. 18.

• 169

  “The program increases total hours worked per week by 4.1 in 2010 and 5.5 in 2012—a 17% increase in labor supply relative to controls both years.” Blattman, Fiala, and Martinez 2013, pg. 20.

• 170

  “This increase is almost entirely in skilled trades. Treatment also results in a very small but statistically significant increase in high-skill wage labor, which includes teaching, health work, government jobs, or other semi-skilled wage work. As a consequence, by 2010, 44% of the treatment group report at least one hour worked in a skilled trade, rising to 48% by 2012. Thus participation and hours in a skilled trade are 2 to 2.5 times greater than in the control group.

  The treatment group does not decrease their hours in other activities, however. Agricultural hours rise at the same rate in the treatment and control groups. Moreover, even in 2012, the treatment group still works twice as many hours in agriculture hours as skilled work. Trades remain a supplement to income, and young adults are primarily engaged in agriculture. Only 7% of the treatment group report 30 or more hours a week in a trade, 4 pp more than the control group. Most are simply adding this new high-skill trade to their portfolio of work activities.” Blattman, Fiala, and Martinez 2013, pg. 20.

• 171
  • ”Assignment to receive a YOP grant increases earnings by UGX 14,605 ($8.50) in 2010 and UGX 18,186 ($10.50) in 2012—increases of 41% and 38% relative to controls (Table III).” Blattman, Fiala, and Martinez 2013, pg. 22.
  • Even though the absolute difference between treatment and control group earnings increased from 2010 to 2012, the difference slightly decreased in percentage terms. This is because average control group earnings increased by 40% over the two year period. “The control group reports monthly cash earnings of approximately UGX 30,825 ($18) in 2008, UGX 35,200 ($20) in 2010 and UGX 47,800 ($28) in 2012.19 Such growth may come in part from a growing economy, but also arises from young people who are gradually increasing their capital stocks and output over time by investing earnings.” Blattman, Fiala, and Martinez 2013, pg. 22.

• 172
  • “We estimate these earnings impacts represent an average annual return on investment (ROI) of 30 to 50%. The 2010 and 2012 earnings ITT estimates in Table III represent ROIs of 30% and 39% on the per capita grant.21 The 2010 and 2012 TOT estimates represent ROIs of 36% and 49%. If we adjust earnings to remove “wages” for additional labor supplied, the treatment effects and ROIs are equal or greater.22 All these ROIs are large relative to the real commercial lending rates of 10 to 30% common among medium-size firms in Uganda. They also approach the ROIs estimated from cash grants to existing microenterprises in Sri Lanka, Mexico, and Ghana (de Mel et al., 2008; McKenzie and Woodruff, 2008; Udry and Anagol, 2006).” Blattman, Fiala, and Martinez 2013, pg. 24.
  • This estimate of the program’s ROI assumes that the cost of the grant was the only cost of the program. We do not know anything about the administrative costs of the program, including facilitating applications, but would guess that they are low relative to the cost of the grant.
  • The ROI estimate is meant to be a measure of the grant’s permanent effect on income. We would guess that earnings gains that have been maintained four years after the grant was distributed will be maintained indefinitely. However, there is evidence that some treatment group members divested from the grant, which could lead income gains to dissipate over time. See later in this page for more discussion of divestment.

• 173

  “Assignment to receive a YOP grant increases earnings by UGX 14,605 ($8.50) in 2010 and UGX 18,186 ($10.50) in 2012—increases of 41% and 38% relative to controls (Table III). We cannot reject the hypothesis that the earnings treatment effect is equal at both endlines. If we divide earnings by hours worked to calculate an average “wage”, we see it is very low—UGX 500 to 850, or $0.29 to 0.49—and it does not increase significantly as a result of treatment (Table III). This implies that earnings gains come from increasing inputs, not productivity.” Blattman, Fiala, and Martinez 2013, pgs. 22-23.

• 174
  • The measure of durable assets is “a z-score constructed by taking the first principal component of 70 measures of land, housing quality, and household assets.” Blattman, Fiala, and Martinez 2013, pg. 22.
  • ”The control group’s durable assets rise by 0.1 SD from 2008 to 2010, and rise by 0.21 SD from 2010 to 2012 (Tables II and III). The indices use the same assets and weights at each survey for comparability. The program impacts are of similar magnitudes: durable assets are 0.10 SD greater than the control group in 2010 and 0.18 SD greater in 2012.” Blattman, Fiala, and Martinez 2013, pg. 23.
  • The measure of non-durable consumption is “a z-score constructed by taking the first principal component of 30 select food items consumed in the past three days and expenditures on 28 select non-food items.” Blattman, Fiala, and Martinez 2013, pg. 22.
  • ”The impact of the program on non-durable consumption in 2012 is identical, 0.18 SD.” Blattman, Fiala, and Martinez 2013, pg. 23.
  • Finally, at both endlines the program increases subjective well-being by 12 to 13% relative to controls. Blattman, Fiala, and Martinez 2013, pg. 23.
  • For difference in mean subjective well-being scores, see Blattman, Fiala, and Martinez 2013 Table III. Treatment improved subjective well-being by 0.4 points on a scale from 1 to 9.

• 175
  • ”Our measures are based mainly on existing measures and include indices of: (1) kin integration, capturing four measures of household relations; (2) community participation, capturing ten measures of associational life and collective action; (3) community public good contributions (2012 only) including seven types of goods; (4) anti-social behavior, based on eight forms of aggressive behavior with neighbors, community leaders, and police, plus 18 additional measures in 2012; and (5) protest attitudes and participation, based on 7 measures of participation in and attitudes around violent anti-government protests following the 2011 elections.
    Overall, we see little evidence of a positive social impact on males after two years, and none whatsoever after four years. Table VIII reports impacts on the main outcome families (disaggregated summary statistics and treatments effects are reported in Appendix B.9). The point estimates are typically less than 0.1 or 0.05 SD, and standard errors on these z-scores are equally small, suggesting we can rule out medium to large changes. Just two of the 27 regressions show a small, statistically significant impact, and both at the 2-year endline. We regard these as at best temporary effects and probably statistical anomalies.” Blattman, Fiala, and Martinez 2013, pgs. 26-27.
  • ”Admittedly, our data have limitations: they are self-reported, and there were no major episodes of unrest to measure. We also did not measure every possible externality, especially collective or general equilibrium changes that accompany broader structural change. Nonetheless, the absence of a large change on the individual margin runs counter to many expectations.” Blattman, Fiala, and Martinez 2013, pg. 27.

• 176

  “A third limitation is that we are unable to evaluate the non-cash components of YOP. We speculate that the group and business plan may have been important as initial commitment devices, though the sustained investment and earnings growth we see over four years suggests that such restrictions were not vital to long-term success. Alternatively, these restrictions may have helped screen out applicants uninterested in becoming artisanal entrepreneurs.” Blattman, Fiala, and Martinez 2013, pg. 27.

• 177

  The government invited young adults to form village groups and prepare a proposal for how they would use a grant to train in and start an independent trade. Blattman, Fiala, and Martinez 2013, pg. 1.

• 178

  ”In the end, YOP appears to have reached a group of motivated, able young people, who on average were neither exceptionally poor nor uneducated relative to their peers, in an economy with little financial depth but bouncing back from civil strife. Our conceptual framework suggests this is exactly the group to benefit from a windfall. This was not entirely accidental—the requirements to form groups, prepare proposals, and wait a long period of time before any grant, with a low probability of success, were designed in part to allow patient, able people with an affinity for vocations to signal their “type”. This may have been the most important function of the groups and proposal in terms of ensuring that the grants were channeled into new employment.” Blattman, Fiala, and Martinez 2013, pg. 27.

• 179

  “We speculate that the group and business plan may have been important as initial commitment devices, though the sustained investment and earnings growth we see over four years suggests that such restrictions were not vital to long-term success.” Blattman, Fiala, and Martinez 2013, pg. 2.

• 180

  “Per capita grant size varied across groups due to variation in group size and amounts requested. 80% of grants were between $200 and $600 per capita, averaging $382.“ Blattman, Fiala, and Martinez 2013, pg. 8.

• 181
  • ”Table IV also reports changes in capital stock levels over time. From 2010 to 2012 the treatment group’s capital stock falls 19%, overall and with both genders. This decline is not statistically significant, however.

    Nonetheless, some in the treatment group do divest substantially. 89% of the treatment groups received a grant but only 68% of treatment group members report enrolling in training and, from Table III, only 48% of the treatment group worked any hours in a skilled trade in the month before the 2012 survey. Thus nearly half of the treated (and a third of those who trained in a trade) are not practicing a trade four years later. Table IV reports changes in capital stock over time in four endogenous subgroups. First, the 11% of the treatment sample who did not receive a grant look much like the control group in that capital stocks rise steeply over time as they accumulate through retained earnings. Second, the 21% who were funded but did not train have capital stocks close to the level of the control group in 2010 and 2012, suggesting that they did not participate meaningfully in the group grant. Their capital stocks rise over time, perhaps due to accumulation of retained earnings. Third, the 48% who were funded, trained, and still practice the trade in 2012 have capital stocks that hold basically steady, declining only 7%. Finally, the 20% who were funded and trained but did not practice a trade in the month before the 2012 survey see their capital stocks decline precipitously back to the level of the control group. These may be the “low ability” or impatient types in our conceptual framework, who find it optimal to divest. We consider alternative explanations in Section 7.” Blattman, Fiala, and Martinez 2013, pg. 19.

  • ”Several patterns suggest that the sample should see substantial growth over time: the regional economy is growing; earnings growth barely slows between the first and second endlines, and the average treatment person is still not fully employed after four years. We do not, however, see sustained growth in capital stocks in the treatment group, even though the treatment group enjoyed robust and rising earnings that could be used to expand the enterprise.

    Does failure to do so mean that the treatment group may have reached their steady state level of capital, and will taper in their growth in the future? It is possible the program brought the average person to their efficient scale given their current entrepreneurial abilities. Half of the treated do not divest, but neither do they grow their capital stock. The treatment group may have yet to take full advantage of their initial capital investments, even after four years. The increase in the earnings treatment effect between the two endlines while labor and capital inputs stay roughly constant is consistent with this interpretation. Only future follow-up of the sample will tell.” Blattman, Fiala, and Martinez 2013, pgs. 31-32.

• 182

  “In 2008 they were 25 years on average, mainly aged 16 to 35.” Blattman, Fiala, and Martinez 2013, pg. 11.

• 183

  “We have comparable population data on age, gender, urban status, marital status, schooling, household size, durable assets, main occupation, and district. We can estimate the PATE by reweighting our sample to reflect the distribution of these characteristics. Since 85% of our sample is aged 18 to 30, we first calculate a PATE for this age range alone, mainly adjusting for the fact that the general population is somewhat poorer and less educated. Investment and earnings treatment effects among 18 to 30 year olds are broadly similar in the population and the sample, though the PATE is marginally (but not statistically significantly) lower. If we consider the full age range, the PATE primarily reweights the treatment effects to older persons. Employment impacts are comparable and the estimated effect on durable assets increases, but the business asset and earnings PATEs are much smaller, and not statistically significant. Full results are in Appendix B.3. We treat these results with caution, however, since young adults are selected into our sample because of unobserved initiative, connections or affinity for entrepreneurship. Thus the PATE probably overstates the true population average treatment effect.” Blattman, Fiala, and Martinez 2013, pgs. 24-25.

• 184

  “The empirical strategy for the evaluation consisted of a randomized experimental design and mixed methods data collection. Following the baseline survey with all 1,800 beneficiaries in mid-2009, IPA held public lotteries in Gulu and Kitgum to randomly assign the 120 program villages to Phase 1 or Phase 2 (stratified by district). In this wait-list control design, all beneficiaries were guaranteed to receive the program, but not all at once. By serving 900 beneficiaries per phase, AVSI had to scale-up their program by 300 percent. Therefore, it was not possible to serve all intended beneficiaries at once.” Blattman et al 2013, pg. 5.

• 185
  • Business skills training. “AVSI provides a brief course in basic business skills for all participants. This course typically runs for five days and covers topics necessary for the planning, starting, and managing of simple business activities. The curriculum has been adapted for illiterate users and AVSI staff is experienced in effectively working with illiterate beneficiaries, who are the majority of the target group of this proposed program. Trainers are AVSI staff members with years of experience in the psychosocial and livelihoods sector and with specific training in business skills, group dynamics and problem solving within the world of business.” Blattman et al 2013, pg. 3.
  • Business plans and grants. ”Clients submit business plans to the AVSI team after the training. Each plan is reviewed and discussed with the client. Upon approval, the client is eligible for a start-up grant. . . .

    All clients receive a start-up grant of approximately $150 USD to be used for the implementation of approved business plans. In the past, this money has been disbursed all at once and in several tranches.” Blattman et al 2013, pgs. 3-4.

  • Follow-up. “AVSI understands that the importance of follow-up visits to the individual and the groups is important from two sides: the inter-personal and the business dimension. Many years of experience have demonstrated to AVSI that on-going support for young, new entrepreneurs is essential to help them succeed and address the challenges that arise with every nascent business endeavor. Clients receive at least three follow up visits.

    On the business side, AVSI staff maintains close supervision of business activities for the first few business cycles, providing advice on meeting market challenges and implementing sound business practices. AVSI staff have been trained in business skills and most importantly have years of experience within the environment of small enterprises in the specific geographic districts of this program, with accumulated links to successful businesses and an array of formal and informal financial services.” Blattman et al 2013, pg. 4.

• 186

  ”Support for Business Networks. AVSI’s experience with this program model suggested that the target women lack support networks that they could use for business advice, savings and lending, and other support. Development programs commonly form villagers, especially women, into groups for this purpose. It is universal, yet untested. We wanted to test whether this was an effective way to increase success and well-being. Therefore in the 60 Phase 1 villages we instituted a cross-cutting design (CCD), where women in 30 of the Phase 1 villages were encouraged to form a mutual support group, elect a leadership, and hold regular meetings. The groups received two days of advising and team building exercises. When we conduct the interim survey at the end of Phase 1, we will be able to measure the impact of these women’s support networks on all of our outcomes of interest.” Blattman et al 2013, pg. 5.

• 187

  “Phase 1 started in mid 2009 and Phase 2 began in early 2011 following the endline survey of all 1,800 beneficiaries in November 2010. By comparing the beneficiaries in Phase 1 to those in Phase 2, who had not received the program at the time of the endline survey, we were able to estimate the medium-run impacts of the program on our core outcomes of interest: sustained livelihoods, poverty, empowerment, gender-based violence, family education and health, and psychosocial well being.” Blattman et al 2013, pg. 5.

• 188

  “Phase 1 started in mid 2009 and Phase 2 began in early 2011 following the endline survey of all 1,800 beneficiaries in November 2010.” Blattman et al 2013, pg. 5.

• 189

  One-third received 2 visits and one-third received five visits. “To the best of our knowledge, the economic and social impacts of follow-up support to recipients of economic assistance programs like WINGS has not been rigorously evaluated. The most relevant literature may be the role and impact of loan officers in microfinance programs, but the evidence base is very limited (Siwale & Ritchie, 2011). Given the logistical challenges and high cost of facilitating multiple home visits and monitoring, it is important to demonstrate the cost-effectiveness of this component of the program. In the second phase of the study, beneficiaries were randomized to receive 0 follow-up visits, 2 visits, or 5 visits to estimate the effect of follow-up ‘dose’. In addition to studying the impact of dose, we also attempted to tease apart the mechanism of follow-up impact—‘accountability’ versus longer-term advising and relationship building—by examining differences in early spending decisions based on beneficiaries’ expectations of follow-up.” Blattman et al 2013, pgs. 5-6.

• 190

  “At the start of the program, AVSI worked with leaders in 120 communities in Gulu and Kitgum districts to identify and screen 2,300 potential beneficiaries. Following this initial assessment, AVSI selected 1,800 of the most vulnerable residents between the ages of 14 and 30 (86% female), approximately 15 per program community. “ Blattman et al 2013, pgs. 3-4.

• 191

  Blattman et al 2013, pg. 9.

• 192

  “Business plans proposed by WINGS recipients were then received and approved by AVSI. Figure 5, taken from an AVSI presentation, shows the breakdown of these approved businesses by type. Over half the businesses centered on the general selling of mixed items, with the rest being dominated by selling of livestock, fish and farm products.” Blattman et al 2013, pg. 12.

• 193

  Blattman et al 2013, pg. 12.

• 194
  • “We presented clients with a pile of stones and a sheet with pictures of twelve kinds of expenditures (which we classify later on into these four categories). Clients were asked to allocate the stones according to how they spent the grant, and the proportions are calculated from the relative balance of stone.” Blattman et al 2013, pg. 38.
  • Blattman et al 2013, pg. 38.

• 195
  • “Both treatment and control groups report about 36,000 UGX (USD 14.49) in spending. . . . The results differ in the level—if the clients had spent a quarter to a third of the grant on business, we would expect 90,000 to 120,000 UGX in spending (USD 36.15 – 48.20).” Blattman et al 2013, pg. 39.
  • According to this survey, about 44% of business expenditures were spent on raw materials and 24% were spent on dues, fees, and other general expenditures. The rest was spent on purchasing inventory, tools or equipment, structural improvement, or materials. Blattman et al 2013, pg. 39.

• 196

  Blattman et al 2013, pg. 16, Figure 9.

• 197
  • The full WINGS program (including follow-up) increased beneficiaries’ monthly net earnings by an average of $6.50. “For the average WINGS beneficiary, net cash earnings increased UGX 16,211 in the month before the survey, a 98% increase over controls. . . . In absolute terms, an increase of UGX 16,211 does not seem large (about $6.50 at market exchange rates of 2500). . . . In absolute terms, an increase of UGX 16,211 does not seem large (about $6.50 at market exchange rates of 2500).” Blattman et al 2013, pgs. 14-15.
  • Using data from phase 2 (where some villages were randomly selected to receive no follow-up visits), Blattman et al 2013 estimate that the follow-up component was responsible for about $2.01 per month of the net earnings increase. “Those assigned to any follow-up report 27% higher cash earnings, a statistically significant increase. In absolute terms the impact is small—about 5,000 UGX per month, or USD 2.01. Since cash earnings are so low in this group, however, the relative impact on the business is substantial.” Blattman et al 2013, pg. 42.
  • We therefore estimate that WINGS increased beneficiaries’ monthly net earnings by $4.49/month ($6.50-$2.01) after the effects of follow-up are subtracted out. Please note that, even after subtracting out follow-up effects, these participants still benefitted from business skills training, the requirement to create a business plan and (in some cases) business networking training in addition to the $150 grant. We are unable to disentangle the effects of these components of WINGS but would guess that the grant was responsible for most of the earnings increase.

• 198
  • Our mean monthly return: $4.49/$150 = 3.0%
  • Our mean annual return: 12*$4.49/$150 = 35.9%
  • These calculations assume that the earnings increases observed after 18 months are permanent. We would guess that this assumption is accurate.
  • Assuming (unrealistically but for the sake of argument) that no services other than the grant had any effect and varying other assumptions about time horizon and discount rate, Blattman et al 2013 estimates that the average lifetime ROI on the $150 grant was between 18% and 1,577%. Blattman et al 2013, pg. 30, Table 4.

• 199
  • According to Blattman et al 2013, pg. 30, Table 4B, the total per-person cost of WINGS (including overhead, follow-up, group dynamics training, business training, targeting & disbursement) was 1,720,063 UGX. The cost of the grant alone was 300,000 UGX and the cost of follow-up was 696,832 UGX (1,658,537 UGX – 961705 UGX). The cost of overhead, group dynamics training, business training, targeting & disbursement was 723,231 UGX = 1,729,063 (cost of entire program) – 696,832 (cost of follow-up) – 300,000 (cost of grant).
  • Therefore, these additional services cost more than double the amount of the grant itself.

• 200
  • “Our household spending measure increases UGX 11,741 (USD 4.72) from the program, which is a 33% increase over the control group (Figure 8).” Blattman et al 2013, pg. 16.
  • WINGS lead to a mean 43% increase in an index of household wealth index and a median 174% increase in that index. Blattman et al 2013, pg. 15, Figure 8.
  • ”Household wealth index: This is an index, scaled 0 to 1, of the household’s durable assets (e.g. furniture) and housing quality, and so reflects wealth and potential for long term consumption and spending.” Blattman et al 2013, pg. 15
  • “We also see an increase in wealth. The absolute value of the index does not have an easy or natural interpretation. It is an approximate ranking of households. The average and median treatment effects are large and positive, and statistically robust, implying that WINGS clients substantially increase their durable assets relative to the control group. We can interpret these results as saying that the increased income from the intervention is channeled largely into short-term as well as durable consumption, raising standards of living.” Blattman et al 2013, pg. 16.
  • “Savings triples on average (sic), going from UGX 40,740 (USD 16.36) to UGX 169,862 (USD 68.22).” Blattman et al 2013, pg. 17.
  • Savings increase by 319% relative to the control group. Blattman et al 2013, pg. 17, Figure 10.
  • Savings increase by $68.22-$16.36 = $51.86.

• 201
  • ”Many of these villages are quite small, and the WINGS client households often represented 15 to 25% of the households.” Blattman et al 2013, pg. 34.
  • “The research team visited all the treatment and control villages after the completion of Phase 1 and surveyed about 2,500 randomly chosen households who did not participate in the WINGS program. The survey collected detailed information on income, entrepreneurial activity, labor supply, savings, as well as consumption and expenditure of non-participant households. Comparing the responses of non-participants in Phase 1 versus Phase 2 villages sheds light on the community-wide effects of the WINGS program.” Blattman et al 2013, pg. 34.

• 202

  “In the realm of the survey, detailed data on community prices was collected, and a price index created. In Phase 1 communities this price index is two percent lower than in Phase 2 communities. This suggests that WINGS increases the supply of scarce traded goods and stimulates competition between microenterprises, driving down consumer prices.” Blattman et al 2013, p. 34.

• 203

  “Preliminary results further suggest that WINGS crowds out profits of existing micro-enterprises. In theory, existing micro-enterprises are affected through two mechanisms. On the one hand, higher competition may crowd-out sales. On the other hand, because WINGS participants spend part of their income gains on consumer goods, sales of existing micro-enterprises may increase. In practice, we find that the former effect slightly dominates the latter. Profits of existing micro-enterprises fall by on average 2,500USH per month (roughly 12 percent). Labor supply of non-participants to micro-enterprise activities, however, is not affected.
  Furthermore, WINGS tends to affect the agricultural labor market. WINGS participants spend less time working on other households’ plots. Lower agricultural labor supply in turn tends to slightly drive up agricultural wages. While WINGS participants spend less time working on other households’ plots, nonparticipant households do spend half a day per month more. This is accompanied by an increase in labor income of 1,200 USH per month. The labor supply effect varies across non-participant households. While households not having a micro-enterprise show an increase of half a day per month, households operating a micro-enterprise spent only a quarter of a day/month more working on other peoples’ plots.” Blattman et al 2013, pg. 35.

• 204

  "We can also compare non-participants in treatment villages to non-participants in control villages (with the caveat that within villages participants were not randomly selected). Overall, despite the size of the program, there are limited spillovers to markets or non-participant households. We see no effect on the incomes or occupational choice of non-participant households, although if we look only at pre-existing traders we see a slight shift from petty trading to casual and agricultural work, with incomes holding more or less steady." Blattman et al 2015, Pg. 24

• 205

  “Examples of community hostility include having serious conflicts with other community members, having community members say things to insult or hurt you or your children, or experiencing unprovoked aggression from other community members. We find that WINGS beneficiaries, on average, report 38.1 percent more hostility than people in the control group. This difference is statistically significant, but it is important to note that this is a very small absolute difference. The community hostility index ranges from a possible score of 0, meaning no hostility experienced, to 12, an indication of high hostility. As shown in Table 3, the mean score among the control group is 0.70, a very low hostility score. Therefore, an increase of 38.1 percent among the treatment group results in a mean score that is still less than 1 on this index.” Blattman et al 2013, pg. 28.

• 206

  “In general, however, we see little health and social effects, positive or negative, of the intervention on beneficiaries, despite the evident poverty impact.” Blattman et al 2013, pg. 23.

• 207

  Carolina Toth, Field Director of GiveDirectly, email to GiveWell, October 24, 2013

• 208
  • “We presented clients with a pile of stones and a sheet with pictures of twelve kinds of expenditures (which we classify later on into these four categories). Clients were asked to allocate the stones according to how they spent the grant, and the proportions are calculated from the relative balance of stone.” Blattman et al 2013, pg. 38.
  • >“Both treatment and control groups report about 36,000 UGX (USD 14.49) in spending. . . . The results differ in the level—if the clients had spent a quarter to a third of the grant on business, we would expect 90,000 to 120,000 UGX in spending (USD 36.15 – 48.20).” Blattman et al 2013, pg. 39.

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  "The data for our analysis come from surveys of stores and households conducted in the experimental villages by the Mexican National Institute of Health both before and after the program was introduced. Baseline data were collected in the final quarter of 2003 and the first quarter of 2004, before villagers knew they would be receiving the program. Follow-up data were collected two years later in the final quarter of 2005, about one year after PAL transfers began in these villages. Our measure of post-program prices comes from a survey of local food stores. Enumerators collected prices for fixed quantities of 66 individual food items, from a maximum of three stores per village, though typically data were collected from one or two stores per village." Cunha, De Giorgi and Jayachandran 2011, Pg 14-15.

• 210

  Cunha, De Giorgi and Jayachandran 2011, Table 2, Pg 35.

• 211

  "Our final data set contains 6 basic PAL goods (corn flour, rice, beans, pasta, oil, fortified milk), 3 supplementary PAL goods (canned fish, packaged breakfast cereal, and lentils), and 51 non-PAL goods" Cunha, De Giorgi and Jayachandran 2011, Pg 15. However, the authors report only the change in prices for the PAL goods.

• 212

  Angelucci and De Giorgi 2009 “To test for effects on the goods market, we first compare prices in treatment and control localities. To do so, we consider village prices by good over time. We provide details on the creation of the price variables in the Appendix, as well as estimates of the price differences between treatment and control villages (Tables A3 and A4). While we find a small positive effect on 5 out of 36 food prices in November 1998, prices of staples such as rice, beans, corn, and chicken do not change. Therefore, we do not expect any substantial increase in the cost of the food basket. Moreover, we find no food price change in the later waves, nor evidence of changes for non-food prices. The evidence presented here is consistent with earlier work by Hoddinott et al. (2000).” Pg 21.

  However, the increases occur in only a small portion of a typical family's basket of goods and only in the first of three follow-up surveys, leading the authors to conclude “that, perhaps with the exception of a minor price increase for some goods in the end of 1998, [Oportunidades] does not significantly change prices in treatment areas.”

  Angelucci and De Giorgi 2009 Online appendix, pg 7. Full quote: “We find a small positive effect on some food prices in November 1998. Prices of onions (p2), lemons (p8), eggs (p26), and coffee (p34) are significantly higher in treatment than in control areas. At the same time, though, the price of fish (p23) is significantly lower. Despite the fact that onions, eggs, and coffee are commonly consumed foods (Hoddinott et al., (2000)), we do not expect these price changes to increase the cost of the food basket substantially, because prices of staples such as rice, beans, corn, and chicken do not change. Second, there is no price change in the later waves. Third, if we consider the pooled waves, the prices of 6 items
  increase, while the prices of 3 goods decrease in the observed time, out of a total of 36 items by 3 waves. This amounts to roughly 8% of good prices changing. We believe that, perhaps with the exception of a minor price increase for some goods in the end of 1998, Progresa does not significantly change prices in treatment areas.”

  Fiszbein and Schady 2009 adds that "The lack of impact on wages and prices of consumer goods is not surprising. In most countries in which CCTs have been evaluated, labor and goods markets are sufficiently developed so that both labor and goods are largely tradable. CCTs may induce larger local demand for goods and lower local supply of labor, and, in the short run, prices may change to reflect these imbalances; in the long run, however, prices should return to their initial equilibrium" (Pg 122).

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  Angelucci and De Giorgi 2009, Table 1.

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  “In the realm of the survey, detailed data on community prices was collected, and a price index created. In Phase 1 communities this price index is two percent lower than in Phase 2 communities. This suggests that WINGS increases the supply of scarce traded goods and stimulates competition between microenterprises, driving down consumer prices.” Blattman et al 2013, p. 34.

• 215
  • ”There are no significant village-level effects on any variable group, suggesting that cash transfers to a group of particularly disadvantaged households within these villages did not impact the general village-level economy.” Haushofer and Shapiro 2013 Policy Brief, pg. 22.
  • Standard errors on these estimates appear relatively large. Haushofer and Shapiro 2013 Policy Brief, pg. 38. However, the study does not include a complete description of how these indices were constructed so we are unsure of whether these estimates include the possibility of meaningful village-level economic effects.

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  “In practice, CCTs appear to have had, at most, modest disincentives for adult work. Two studies (Parker and Skoufias 2000; Skoufias and di Maro 2006) examine the effects of Oportunidades on adult labor supply; neither finds evidence of disincentive effects. The data used by Edmonds and Schady 2011 suggest that the BDH program in Ecuador had no effects on adult labor supply; in a similar vein, Filmer and Schady (2009c) report that adult labor supply was largely unaffected by the CESSP program in Cambodia. Only in Nicaragua is there some evidence of significant negative effects on adult work: [Maluccio and Flores 2005] show that the RPS resulted in a significant reduction in hours worked by adult men in the preceding week (by about 6 hours), with no effect among adult women.” Fiszbein and Schady 2009, Pgs 117-119.

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  • “The program increases total hours worked per week by 4.1 in 2010 and 5.5 in 2012—a 17% increase in labor supply relative to controls both years. This increase is almost entirely in skilled trades. Treatment also results in a very small but statistically significant increase in high-skill wage labor, which includes teaching, health work, government jobs, or other semi-skilled wage work. As a consequence, by 2010, 44% of the treatment group report at least one hour worked in a skilled trade, rising to 48% by 2012. Thus participation and hours in a skilled trade are 2 to 2.5 times greater than in the control group. The treatment group does not decrease their hours in other activities, however. Agricultural hours rise at the same rate in the treatment and control groups. Moreover, even in 2012, the treatment group still works twice as many hours in agriculture hours as skilled work. Trades remain a supplement to income, and young adults are primarily engaged in agriculture. Only 7% of the treatment group report 30 or more hours a week in a trade, 4 pp more than the control group. Most are simply adding this new high-skill trade to their portfolio of work activities.” Blattman, Fiala, and Martinez 2013, pg. 20.
  • Participating in WINGS caused a 61% increase in employment hours, which consisted of a 41% increase in hours spent on subsistence work and a 79% increase in hours spent on market activities. Blattman et al 2013, pg. 16, Figure 9.

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  Haushofer and Shapiro 2013 Policy Brief, pg. 33, Table 5.

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  The evidence we have seen cannot distinguish between:

  • income effects: families using income from conditional cash transfers to offset income from child labor, and therefore reducing the amount of hours worked by children; and
  • conditionality effects: since many conditional cash transfer programs require school attendance in order to qualify for transfers, families may reduce the number of hours worked by children in order to qualify for the transfers.

  These effects differ in that they have disparate predictions for the effects of unconditional cash transfers on child labor.

  Summarizing the evidence, Fiszbein and Schady (2009) states, “several CCTs have been successful in reducing child work. Frequently, these impacts have been concentrated among older children. Table 4.5 shows that Oportunidades reduced child work among older children, aged 12–17, especially among boys (for whom baseline levels of child work also were substantially higher). Skoufias and Parker (2001) also show that domestic work decreased substantially, especially for girls.
  In Ecuador, Edmonds and Schady (2008) shows that the Bono de Desarrollo Humano program had very large effects on child work among those children most vulnerable to transitioning from schooling to work. Those effects are concentrated in work for pay away from the child’s home. BDH transfers, on the other hand, had small effects on child time allocation at peak school attendance ages and among children already out of school at baseline. In Cambodia, the CESSP program, which gives transfers to children in transition from primary to lower-secondary school, reduced work for pay by 11 percentage points (Filmer and Schady 2009c).
  Other CCT programs also appear to have reduced child work. In Nicaragua, the Red de Proteción Social program reduced child work by 3–5 percentage points among children aged 7–13 (Maluccio, John A., and Rafael Flores. 2005). Furthermore, the fraction of children who only studied (as opposed to worked and studied, only worked, or neither worked nor studied) increased significantly (from 59 percent to 84 percent) as a result of the RPS (Maluccio 2005). Yap, Sedlacek, and Orazem (2008) estimate the effects of the Brazilian Programa de Erradicação do Trabalho Infantil (PETI) program, another precursor of the Bolsa Família program. PETI gave out conditional transfers to secondary school-age children enrolled in school. Stipends were given directly to students, not to the families and were conditional on school attendance and participation in special training workshops. PETI beneficiaries reduced substantially their probability of working. Attanasio et al. (2006), however, finds no effect of the Familias en Acción program on child work in Colombia (although the program does appear to have reduced the amount of time dedicated to domestic chores). Glewwe and Olinto (2004) find no effect of the PRAF program on child work in Honduras.

  Two recent papers consider the impact of CCTs on child work when the transfer is conditional on school attendance for only one child in the household and that child has siblings. Programs of this nature could have positive or negative spillovers for other siblings. Positive outcomes include if the income effect reduces child work for all children, if transfers increase the bargaining capacity of women within the household, or if the social marketing by the program leads parents to reduce child work even for children whose school attendance is not monitored. Negative impact could include parents compensating for the reduction in work of one child by increasing the work of other siblings. Barrera-Osorio et al. (2008) analyze Subsidios Condicionados a la Asistencia Escolar, a pilot CCT program in Bogotá, Colombia. This program randomized assignment to individual children rather than households, and made transfers directly to students rather than to their parents. Barrera-Osorio et al. show that, within the same household, a student selected into the program is 2 percentage points more likely to attend school and works about 1 hour less than a sibling who has not been selected; however, the beneficiary’s sibling – particularly if this sibling is a girl – is less likely to attend school than are children in households that received no cash transfer at all. In contast, Filmer and Schady (2009c) find that the CESSP program in Cambodia had no effect on the school enrollment of a beneficiary’s ineligible siblings.” pgs 115-116.

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  Fiszbein and Schady 2009, pg 114, “[T]able 4.1 shows that, for most countries, the impact of the transfer is generally somewhat smaller than the magnitude of the transfer (when both are normalized as a fraction of the consumption or income of households in the control group). The difference between these two values may be a result of behavioral changes by CCT beneficiaries, which partly offset the value of the transfer itself. We now turn to a discussion of the evidence on these possible offsetting effects, focusing on impacts on child labor, adult labor, remittances, fertility, and spillovers and other general equilibrium effects.”

  Other potential explanations might include:

  • reductions in adult labor in favor of increased leisure time
  • increased savings or investment in productive assets
  • errors in measuring consumption, leading to attenuation in the estimated increase associated with receiving cash transfers
  • misappropriation of transfers.

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  Haushofer and Shapiro 2013 Policy Brief, Table 10, Pg 38. Haushofer and Shapiro 2013 Policy Brief's estimate of the program's effects on an index of crime seems to have large standard errors, however. The methodology used to construct the index is not described, so we cannot tell whether the estimate excludes the possibility of large increases in crime.

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  "Additional variables in table 9 show the frequency of any episode of physical, sexual or emotional violence in the last six months, and the percentage of respondents who believe that domestic violence is justified in some instances. The point estimates for these variables suggest a reduction in domestic violence, although none are individually different from zero at conventional significance levels." Haushofer and Shapiro 2013 Policy Brief, Pg 21.
  

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  “Examples of community hostility include having serious conflicts with other community members, having community members say things to insult or hurt you or your children, or experiencing unprovoked aggression from other community members. We find that WINGS beneficiaries, on average, report 38.1 percent more hostility than people in the control group. This difference is statistically significant, but it is important to note that this is a very small absolute difference. The community hostility index ranges from a possible score of 0, meaning no hostility experienced, to 12, an indication of high hostility. As shown in Table 3, the mean score among the control group is 0.70, a very low hostility score. Therefore, an increase of 38.1 percent among the treatment group results in a mean score that is still less than 1 on this index.” Blattman et al 2013, pg. 28.

• 224

  “We investigate the effects of a positive income shock on mental health among adolescent girls using evidence from a cash transfer experiment in Malawi. Offers of cash transfers strongly reduced psychological distress among baseline schoolgirls. However, these large beneficial effects declined with increases in the transfer amount offered to the parents conditional on regular school attendance by the adolescent girls. Improved physical health, increased school attendance, personal consumption, and leisure contributed to the effects. There was also strong evidence of increased psychological distress among untreated baseline schoolgirls in treatment areas. All of these effects dissipated soon after the program ended.” Baird, de Hoop and Ozler 2012, Abstract

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  • “The following are key outcome variables of interest: 1. Prices: how do prices evolve in response to an influx of cash into local economies? 2. Number of enterprises: how does the supply side change in response to a potential increase in demand due to redistribution? 3. Household welfare: how do household income and assets change in response to the cash transfers, both for direct beneficiaries and for non-beneficiaries in the study area? 4. Local public finance outcomes: are there changes in local fundraising for public goods?” General Equilibrium Effects of Cash Transfers in Kenya, AEA RCT Registry
  • “The study will take place across 653 villages in Western Kenya. Villages are randomly allocated to treatment or control status. In treatment villages, GiveDirectly enrolls and distributes cash transfers to households that meet its eligibility criteria. In order to generate additional spatial variation in treatment density, groups of villages are assigned to high or low saturation. In high saturation zones, 2/3 of villages are targeted for treatment, while in low saturation zones, 1/3 of villages are targeted for treatment. The randomized assignment to treatment status and the spatial variation in treatment intensity will be used to identify direct and spillover effects of cash transfers.” General Equilibrium Effects of Cash Transfers in Kenya, AEA RCT Registry
  • ”End date: 2016-12-31” General Equilibrium Effects of Cash Transfers in Kenya, AEA RCT Registry
  • Baseline data collection was slightly slower than expected, which meant that GiveDirectly had to delay some transfers (so that researchers could complete the baseline survey before recipients had received cash). Paul Niehaus and Carolina Toth, conversation with GiveWell, September 7, 2015

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  “This study employs a two-level cluster-randomized controlled trial. An overview of the design is shown in Figure 1. In collaboration with GD, we identified 126 villages from a list of villages in Rarieda district of Western Kenya. In the first stage of randomization, 63 of these villages were randomly chosen to be treatment villages. Within all villages, we conducted a census with the support of the village elder, which identified all eligible households within the village. As described above, eligibility was based on living in a house with a thatch roof. Control villages were only surveyed at endline; in these villages, we sampled 432 households from among eligible households, to which we refer as “pure control” households in the following.
  In treatment villages, we performed a second stage of randomization, in which we randomly assigned 50% of the eligible households in each treatment village to the treatment condition, and 50% to the control condition. This process resulted in 503 treatment households at baseline, and 505 control households in treatment villages, to which we refer as “spillover” households in the following.” Haushofer and Shapiro 2013 Policy Brief, pg. 6.

• 227
  • Haushofer, Reisinger and Shapiro 2015 uses the prefix “USD” to refer to PPP adjusted U.S. dollars.
    • "A conversation in private was then requested from this household member, in which they were asked a few questions about demographics, and informed that they had been chosen to receive a cash transfer of KES 25,200 (USD 404)." Haushofer, Reisinger and Shapiro 2015, Pg. 5
    • "Between 2011 and 2013, the NGO GiveDirectly sent unconditional cash transfers of at least USD 404[1], or at least twice the monthly average household consumption in the area, to randomly chosen poor households in Kenya through the mobile money system M-Pesa." Haushofer and Shapiro 2013, Pg. 2
    • "[1] All USD values are calculated at purchasing power parity, using is the 2012 World Bank PPP estimate for private consumption in Kenya: 0.016." Haushofer and Shapiro 2013, Pg. 2
  • Haushofer, Reisinger and Shapiro 2015 states that the effects on consumption and asset holdings are reported in USD PPP. It does not explicitly state the units of the effects on revenue, but we assume that they are also reported in USD PPP, because consumption and asset holdings are reported in USD PPP and there is nothing in the paper to indicate otherwise.
    • Table A.6.3: Effect on Consumption, "Notes: OLS estimates of the effect of changes in own wealth, thatched village mean wealth, and thatched village inequality on measures of household monthly consumption at endline reported in USD PPP." Haushofer, Reisinger and Shapiro 2015, Pg. 56
    • Table A.6.4: Effect on Assets, "Notes: OLS estimates of the effect of changes in own wealth, thatched village mean wealth, and thatched village inequality on measures of household monthly consumption at endline reported in USD PPP." Haushofer, Reisinger and Shapiro 2015, Pg. 57
    • Table A.6.5: Effect on Labor and Enterprise, It does not mention PPP. Haushofer, Reisinger and Shapiro 2015, Pg. 58
  • Note that Haushofer and Shapiro 2013 Policy Brief uses the prefix “USD” to refer to dollars in exchange-adjusted terms (emphasis ours in the quote below).
    • “Large vs. small transfers Finally, a third treatment arm was created to study the relative impact of large compared to small transfers. To this end, 137 households in the treatment group were randomly chosen and informed in January 2012 that they would receive an additional transfer of KES 70,000 (USD 798, PPP 1,112), paid in seven monthly installments of KES 10,000 (USD 114, PPP 160) each, beginning in February 2012. Thus, the transfers previously assigned to these households, whether monthly or lump-sum, were augmented by
      KES 10,000 from February 2012 to August 20128, and therefore the total transfer amount received by these households was KES 95,200 (USD 1,085, PPP 1,525). The remaining 348 treatment households constitute the “small” transfer group, and received transfers totaling KES 25,200 (USD 287, PPP 404) per household.
      These three treatment arms were fully cross-randomized, except that, as noted above, the “large” transfers were made to existing recipients of KES 25,200 transfers in the form of a KES 70,000 top-up that was delivered as a stream of payments after respondents had already been told that they would receive KES 25,200 transfers. Section 3.1 outlines how this issue is dealt with in the analysis.” Haushofer and Shapiro 2013 Policy Brief, Pgs. 7-8.

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  • “Control villages were only surveyed at endline; in these villages, we sampled 432 households from among eligible households, to which we refer as “pure control” households in the following. . . . To obtain a lower-bound estimate for spillover effects, we compare households which still have thatched roofs at endline to pure control households which still have thatched roofs at endline. The logic behind this choice is the following. First, note that in the absence of spillover effects on roof purchases, this comparison provides an unbiased estimate of the spillover effects for this group of households. Second, relax the assumption of no spillovers and assume instead (as is likely) that spillover effects predominantly induce the better-off control households in treatment villages to upgrade to an iron roof. If this is the case, restricting the sample to households which still have a thatched roof at endline selects for poorer households in treatment villages, but not pure control villages, and thus provides a lower bound estimate of the spillover effect. To be conservative, in what follows we report this lower-bound estimate.” Haushofer and Shapiro 2013 Policy Brief, pgs. 6-7.
  • In total, the study had roughly 900 households in the sample at endline, split roughly evenly between spillover and control households.
    • Haushofer and Shapiro 2013 does not report the number of households actually included in the analysis of spillover effects (i.e., spillover and control households with thatched roofs at endline that had measurements of the relevant outcomes).
    • 901 households in the sample at endline: 469 spillover households at endline and 432 control households at endline. Figure 1, Haushofer and Shapiro 2013, Pg. 45
  • The mean follow-up time between the end of the transfer and the endline survey was 4.3 months; presumably, the same average follow-up time as Haushofer, Reisinger and Shapiro 2015 (discussed below).

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  • More precisely, the study finds:
    • that spillover households had slightly lower consumption, assets, and revenue than control households, but the effects were not statistically significant and were imprecisely estimated; there was an average difference of -$19 (95% CI: -$60 to $23) in monthly non-durable expenditure relative to average monthly non-durable expenditure of $157 in control households, -$8 (95% CI: -$22 to $7) in the value of non-land assets relative to average non-land assets of $478 in control households, -$5 (95% CI: -$16 to $6) in total monthly revenue relative to average revenue of $49 in control households.
      • Column (3), Table 1, Haushofer and Shapiro 2013, Pg. 49
    • an average difference of 0.08 (95% CI: -0.06 to 0.22) standard deviations in an index of psychological well-being (i.e., an increase in well-being for spillover households relative to control households equal to about 40% of the direct benefit found for treatment households, though not statistically significant and imprecisely estimated)
      • Column (3) (“Spillover effect”), Table 1, Haushofer and Shapiro 2013, Pg. 49
      • 0.20 (p < 0.01), Column (2) (“Treatment effect”), Table 1, Haushofer and Shapiro 2013, Pg. 49
  • The study found highly statistically significant increases of $36, $279, and $17 in monthly non-durable expenditure, the value of non-land assets and total monthly revenue respectively for treatment households compared to the spillover households.
    • Column (2), Table 1, Haushofer and Shapiro 2013, Pg. 49
  • The study found that treatment improved an index of psychological well-being by 0.45 standard deviations (95% CI: 0.25 to 0.65).
    • Small transfers: 0.11 (95% CI: -0.01 to .23). Table 28, Haushofer and Shapiro 2013 Appendix, Pg. 54

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  • ”There are no significant village-level effects on any variable group, suggesting that cash transfers to a group of particularly disadvantaged households within these villages did not impact the general village-level economy.” Haushofer and Shapiro 2013 Policy Brief, pg. 22.
  • Standard errors on these estimates appear relatively large. Haushofer and Shapiro 2013 Policy Brief, pg. 38. However, the study does not include a complete description of how these indices were constructed so we are unsure of whether these estimates include the possibility of meaningful village-level economic effects.

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  • "The data used in this study derives from a randomized controlled trial conducted in collaboration with GiveDirectly, Inc. (GD; www.givedirectly.org), a not-for-profit organization which makes unconditional cash transfers to poor households in Kenya and Uganda. In this section, we discuss the details of GiveDirectly’s protocol for making cash transfers, design of the experiment, and data collection methods. Further details on study design can be found in the paper reporting the main treatment effects of the program Haushofer and Shapiro (2013)." Haushofer, Reisinger and Shapiro 2015, Pg. 4
  • "To isolate exogenous variation in relative wealth by village, we use variation in the treatment intensity across villages. The variation in this measure stems from two sources: first, the proportion of treated households varied around the targeted 50 percent across villages, leading to differences in the average transfer amount across villages. While the original intent of the program was to treat exactly 50 percent of eligible households in each village, some variation still exists. This is largely due to the fact that in many villages only a small number of households were eligible, and often the number of eligible households was odd, precluding a clean split. Thus the proportion of eligible households receiving a transfer ranges from 40 percent to 75 percent.
    Second, the proportion of households receiving large (as opposed to small) transfers varied randomly across villages. After being selected to receive a transfer, 137 households were then randomly designated to receive a large transfer, without enforcing an equal split by village. Table A.1.4 in the Appendix details the proportion of treated households in each village receiving large transfers. The mean across villages was 27 percent, ranging from 0 percent to 57 percent." Haushofer, Reisinger and Shapiro 2015, Pg. 9
  • Haushofer, Reisinger and Shapiro 2015 also analyzes variation in the size of the cash transfer given to households and in the average baseline wealth of households.
    • “To isolate exogenous variation in absolute wealth, we use the total amount of the transfer received by each household. Since households were assigned to a control condition or to receive small or large transfers, this variable takes a value of USD 0, USD 404, or USD 1525.” Haushofer, Reisinger and Shapiro 2015, Pg. 8
    • ”To isolate exogenous variation in the dispersion of wealth by village, we calculate the change in the village-level inequality level induced by the transfers. The variation in inequality arises from the fact that significant variation exists in the average baseline wealth (as measured by self-reported total assets) of households selected to receive a transfer by village. As shown in Figure A.1.3 in the Appendix, the village-level average of the asset holdings of treated households ranged from USD 136 to USD 1026 (mean USD 383). Due to random assignment of treatment among these households, in some villages the mean baseline wealth level of treated households is relatively low, while in others it is relatively high. If more of the relatively poor households in a village receive transfers, then inequality within the sample population is likely to decrease. Conversely, if the mean baseline wealth level of treated households in a village is relatively high, then inequality in the sample population is likely to increase.” Haushofer, Reisinger and Shapiro 2015, Pg. 11

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  • In actuality, the analysis was more complex; an example of one of the authors’ regressions follows. For a given economic outcome, the authors ran a regression of the outcome at endline on (a) the cash transfer amount for the household, (b) the average cash transfer amount per eligible household for the village in which the household resides, (c) the Gini coefficient (a measure of inequality) for the village in which the household resides, and (d) other control variables.
    • Equations (1)-(2), Haushofer, Reisinger and Shapiro 2015, Pg. 14
    • “Column (7) reports the sample size. The unit of observation is the household”, Tables A.6.3-A.6.5, Haushofer, Reisinger and Shapiro 2015, Pgs. 56-58
  • The authors ran an analogous regression for the psychological well-being index, but at the level of the individual instead of the household.
    • Equations (1)-(2), Haushofer, Reisinger and Shapiro 2015, Pg. 14
    • “Column (7) reports the sample size. The unit of observation is the individual”, Table 1, Haushofer, Reisinger and Shapiro 2015, Pg. 29
  • In total, it measured economic outcomes for around 900 households and psychological well-being outcomes for around 1500 individuals.
    • “Column (7) reports the sample size. The unit of observation is the individual”, Table 1, Haushofer, Reisinger and Shapiro 2015, Pg. 29
    • “Column (7) reports the sample size. The unit of observation is the household”, Tables A.6.3-A.6.5, Haushofer, Reisinger and Shapiro 2015, Pgs. 56-58
  • Also, though we refer to “average transfer size in a village” above, we more precisely mean “average transfer size per eligible household in a village.” By “similar households”, we more precisely mean comparing households that received similarly sized cash transfers (or did not receive cash transfers) with similar values for the control variables included in the regression living in villages with similar levels of inequality (as captured by the Gini coefficient) but with different average transfer sizes per eligible household.

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  • An effect that we don’t include in the body of our discussion of this study is that the study finds no evidence that changing village-level inequality impacts psychological well-being, non-durable expenditure, asset holdings or revenue. However, the study does find that increasing village-level inequality (while holding the average transfer size per eligible household in a village and many other variables constant) leads to a statistically significant decrease in the proportion of households whose main source of income is wage labor. However, this effect does not play an important role in our view because (a) we are uncertain whether cash transfers are more likely to increase or decrease village-level inequality (though we would guess they are more likely to decrease inequality), (b) we are uncertain whether to see a shift toward wage labor as positive or negative in this particular context (though we would guess it is positive), (c) we have no evidence from the study that increases in inequality would impact any of the other economic outcomes measured (e.g., consumption, assets, and revenue), and (d) we find interpreting the effects of changes in inequality while controlling for the size of a household’s cash transfer and the average transfer per household in the village particularly complex and so are hesitant to place a lot of weight on this finding.
    • Psychological well-being: “We detect no statistically significant effect of a change in thatched village inequality on psychological wellbeing in the full sample population, as reported in columns (5) and (6). However, we cannot rule out the possibility that the present study is underpowered to detect these effects, or that these inequality measures do not accurately reflect the change in inequality for the entire village as discussed in Section 2.4.” Haushofer, Reisinger and Shapiro 2015, Pg. 18
    • There are statistically insignificant estimates with very wide confidence intervals for the effect of increasing inequality on monthly non-durable expenditure, the value of non-land assets and total monthly revenue (Column (6), Table A.6.3-A.6.5, Haushofer, Reisinger and Shapiro 2015, Pgs. 56-58)
    • Wage labor: “Finally, we also observe effects of changes in village-level inequality on labor and enterprise outcomes. As reported in columns (5) and (6) of Table A.6.5, as inequality rises, households are significantly less likely to engage in wage labor as their primary source of income. This effect is significant at the 5 percent level without controls, and with control is significant at the 1 percent level and at the 5 percent level after FWER correction. For a 0.07 change in the village-level Gini coefficient we predict a 4 percentage point decrease in the proportion of households whose main source of income is wage labor.” Haushofer, Reisinger and Shapiro 2015, Pg. 18
    • Extrapolating the wage labor finding to GiveDirectly: We would guess that GiveDirectly’s program decreases inequality by giving transfers to all thatched roof households in a village, which tend to be poorer. If GiveDirectly’s program decreases inequality, the study’s findings imply that GiveDirectly’s program would increase the proportion of households whose main source of income is wage labor.
    • Average absolute magnitude of the change in Gini coefficient: “The average baseline Gini coefficient was 0.43, and the average absolute magnitude of the change in Gini was 0.075, ranging from a decrease of 0.17 to an increase of 0.21 (note that some villages may be outliers due to the relatively small number of households included in the sample).” Haushofer, Reisinger and Shapiro 2015, Pgs. 11-12
    • Average Change in Gini Coefficient: 0.01, Haushofer, Reisinger and Shapiro 2015, Pg. 33
    • Measure of inequality used: “Following our pre-analysis plan, we use two alternate measures of inequality. Our primary measure is the change Gini coefficient calculated using PPP adjusted total household nondurable assets for thatched roof households in each village.” Haushofer, Reisinger and Shapiro 2015, Pg. 11

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  • It found a regression coefficient corresponding to a -0.05 (95% CI: -0.13 to 0.03) change in an individual’s psychological well-being index for every $100 increase in the average cash transfer amount per eligible household for the village in which the individual lives. Column (4), Table 1, Haushofer, Reisinger and Shapiro 2015, Pg. 29
  • As a point of comparison, the study found a regression coefficient corresponding to a 0.03 (p < 0.01) standard deviation increase in an individual’s psychological well-being index for every $100 increase in the cash transfer amount for the household in which the individual lives. Column (2), Table 1, Haushofer, Reisinger and Shapiro 2015, Pg. 29
  • For a description of the regression done in Haushofer, Reisinger and Shapiro 2015, see the above footnote.
  • Haushofer, Reisinger and Shapiro 2015 found no apparent effect on the individual components of the psychological well-being index except for life satisfaction. The effect on life satisfaction is not statistically significant when accounting for multiple comparisons. However, the study also does a subgroup analysis on only households that did not receive transfers in which the effect on life satisfaction is statistically significant; the other components of the well-being index remain non-significant in the subgroup analysis (Column (2), Table 2, Haushofer, Reisinger and Shapiro 2015, Pg. 30). Effects for the analysis of the full sample are below:
    • Column (4), Table 1, Haushofer, Reisinger and Shapiro 2015, Pg. 29
    • Life satisfaction: -0.09 (95% CI: -0.17 to -0.01) standard deviation change (p-value of 0.12 when accounting for multiple comparisons)
    • Happiness: 0 (95% CI: -0.06 to 0.06) standard deviation change
    • Depression: -0.01 (95% CI: -0.09 to 0.07) standard deviation change
    • Stress: 0.06 (95% CI: -0.04 to 0.16) standard deviation change
    • Log cortisol: -0.01 (95% CI: -0.07 to 0.05) standard deviation change
  • We are uncertain about the magnitude of the absolute changes in the psychological well-being index and its components. For example, we are uncertain about whether a 0.09 standard deviation decrease in life satisfaction corresponds to a small or large change in the absolute level of an individual’s life satisfaction (e.g., a large change would be moving from a “6” to an “8” on a life satisfaction scale from 1 to 10). Haushofer, Reisinger and Shapiro 2015 describe their procedure for constructing the outcome variables related to psychological well-being: “Each of these outcome variables is standardized by subtracting the control group baseline mean and dividing by the baseline control group standard deviation5” (Pg. 8). The paper only reports these standardized scores. If the baseline control group standard deviation was small, then one might see large changes in the standardized scores with little change in the absolute level of psychological well-being for individuals.

• 235
  • Note that the authors find that the positive psychological effects of receiving a cash transfer seem to fade over time as well, though they remain positive and significant when including the full 15 months of follow-up.
  • "An important question in light of these results is how long the negative psychological externalities of cash transfers persist. As discussed in Section 2.3.4, we are able to exploit variation in the timing of transfers over the course of the study to determine the effects of transfers received closer to the endline survey. Since the study was scheduled to run for 15 months, we calculate changes in own wealth village mean wealth and village Gini due to transfers in the 1 month before endline, the 2 months before endline, etc., up through the full 15 months before endline. We then perform separate regressions to determine the effects of changes in each of these time periods. Note that these measures are overlapping (e.g., the transfers 1 month before endline are a subset of of the transfers 2 months before endline), so these measures are not fully independent.
    However, the results depicted in Figures 2 and Appendix Table A.4 are illustrative of a clear trend. The values of change in household wealth and village mean wealth due to the most recent transfers show a much stronger effect on each measure of psychological well-being, with the effects diminishing as we begin to include transfers closer to the beginning of the period. For the well-being index, we see a point estimate for the negative effect of a USD 100 change in village mean wealth due to transfers in the 1 month before endline greater than 0.4 SD, but the point estimate is indistinguishable from 0 when we include transfers over the full 15 months. Similarly, a change in own wealth of USD 100 in the month before endline causes a nearly 0.2 SD increase in the psychological well-being index, but this effect decreases (though it remains positive and significant) when including the full 15 months. Similar results hold for the other variables, though many of the effects are quite noisy.
    Overall, the fact that the effects of transfers early on in the program drown out the effects shortly before endline is evidence that the psychological effects of cash transfers diminish over time." Haushofer, Reisinger and Shapiro 2015, Pg. 20
  • "Index", "Mean", Table A.4.2: Effect of Recent Transfers, Haushofer, Reisinger and Shapiro 2015, Pg. 45
  • “Thus, at the average level of village wealth change (USD 354), an individual would report a decrease in life satisfaction of 0.33 SD. This is in comparison with an increase in life satisfaction of 0.13 SD at the average transfer amount (USD 709), implying a net decrease in life satisfaction for households that either did not receive transfers or that received small transfers, and a negation of the positive direct effect of transfers on households receiving large transfers.” Haushofer, Reisinger and Shapiro 2015, Pgs. 17-18

• 236
  • “However, the results depicted in Figures 2 and Appendix Table A.4 are illustrative of a clear trend. The values of change in household wealth and village mean wealth due to the most recent transfers show a much stronger effect on each measure of psychological well-being, with the effects diminishing as we begin to include transfers closer to the beginning of the period. For the well-being index, we see a point estimate for the negative effect of a USD 100 change in village mean wealth due to transfers in the 1 month before endline greater than 0.4 SD, but the point estimate is indistinguishable from 0 when we include transfers over the full 15 months. Similarly, a change in own wealth of USD 100 in the month before endline causes a nearly 0.2 SD increase in the psychological well-being index, but this effect decreases (though it remains positive and significant) when including the full 15 months. Similar results hold for the other variables, though many of the effects are quite noisy.
    Overall, the fact that the effects of transfers early on in the program drown out the effects shortly before endline is evidence that the psychological effects of cash transfers diminish over time." Haushofer, Reisinger and Shapiro 2015, Pg. 20

• 237
  • The study found regression coefficients corresponding to a -$7 (95% CI: -$16 to $1), -$36 (95% CI: -$72 to $0), and -$6 (95% CI: -$15 to $3) change in a household’s monthly non-durable expenditure, asset holdings and revenue respectively for every $100 increase in the average cash transfer amount per eligible household for the village in which the household resides.
    • Column (4), Tables A.6.3-A.6.5, Haushofer, Reisinger and Shapiro 2015, Pgs. 56-58
  • It is not straightforward to make these effect sizes easily comprehensible. However, as a rough point of comparison: there was average monthly non-durable expenditure of $157 in control households in Haushofer and Shapiro 2013, average non-land assets of $478 in those control households, and average revenue of $49 in those control households. If a village received a $354 increase in the average cash transfer amount per eligible household in the village, the above findings roughly imply that spillover households in those villages would lose about -$25, -$127, and -$21 in monthly non-durable expenditure, asset holdings and revenue respectively. These are decreases of about 16%, 27%, and 43% in monthly non-durable expenditure, asset holdings and revenue respectively (assuming that spillover households are similar to control households in their baseline consumption, assets, and expenditure). These estimates imply even larger potential negative spillover effects of GiveDirectly’s core program (which provides larger transfers than were provided in the RCT). We also assume in this analysis that any changes in inequality induced by this increase in village mean wealth do not have an effect on these economic outcomes, which seems reasonable given that the study reported statistically insignificant estimates of the effects on these outcomes with very wide confidence intervals (Column (6), Tables A.6.3-A.6.5, Haushofer, Reisinger and Shapiro 2015, Pgs. 56-58).
    • Column (3), Table 1, Haushofer and Shapiro 2013, Pg. 49
    • -7*3.54=-24.8; -36*3.54=-127.4; -6*3.54=-21.2
    • 24.8/157=15.8%; 127.4/478=26.7%; 21.2/49=43%
    • “...at the average level of village wealth change (USD 354)...” Haushofer, Reisinger and Shapiro 2015, Pgs. 17-18
  • It is not straightforward to compare these effect sizes to Haushofer and Shapiro 2013. However, a rough comparison of the predictions from Haushofer, Reisinger and Shapiro 2015 at the average increase in village mean wealth to the lower bounds of the 95% confidence intervals (i.e., the most negative effects within the 95% confidence interval) of the spillover effects from Haushofer and Shapiro 2013 suggests that the findings of Haushofer, Reisinger and Shapiro 2015 imply larger negative effects than Haushofer and Shapiro 2013. The lower bounds of the spillover effects (i.e., the effect of the transfer program on spillover households’ consumption, assets, and revenues) from Haushofer and Shapiro 2013 are -$22, -$60 and -$16 for monthly non-durable expenditure, asset holdings and revenue respectively (Column (3), Table 1, Haushofer and Shapiro 2013, Pg. 49) and are lower than the point estimate predictions at the average increase in village mean wealth from Haushofer, Reisinger and Shapiro 2015 (see the bullet point above).
  • As another point of comparison, the following describes the estimated positive effects for households receiving a transfer: The study found regression coefficients corresponding to a $3.35 (p < 0.01), $34.44 (p < 0.01), $1.10 (p < 0.10) change in a household’s monthly non-durable expenditure, asset holdings and revenue respectively for every $100 increase in the cash transfer amount for the household. At the average transfer size of $709 (“At the mean transfer amount of USD 709, … ” Haushofer, Reisinger and Shapiro 2015, Pg. 17), the regression model predicts an increase of $24, $244 and $8 for a household’s monthly non-durable expenditure, asset holdings and revenue respectively.
    • Column (2), Tables A.6.3-A.6.5, Haushofer, Reisinger and Shapiro 2015, Pgs. 56-58
  • Haushofer and Shapiro 2013 found somewhat higher direct effects of $36, $279 and $17 on a household’s monthly non-durable expenditure, asset holdings and revenue respectively comparing treatment households to spillover households (Column (2), Table 1, Haushofer and Shapiro 2013, Pg. 49). However, if the negative spillover effects from Haushofer, Reisinger and Shapiro 2015 are real, then the positive effects found in Haushofer and Shapiro 2013 would have been overestimated (to determine the direct benefits of transfers to households, Haushofer and Shapiro 2013 compares treatment households to spillover households).

• 238

  “The exact mechanism explaining this decrease is not immediately apparent, as the decrease appears to be consistent across categories (other than marginal increases in alcohol and tobacco spending). One possibility may be that as mean village wealth rises, households substitute away from consumption and towards investment. However, we also observe a decrease in overall asset levels, as reported in columns (3) and (4) of Table A.6.4, with a USD 100 increase in village mean wealth resulting in a USD 36 decrease in household assets, significant at the 10 percent level9. This decrease is mainly driven by (non-significant) decreases in livestock and durables holdings. One possible explanation for this pattern of results is that households sell livestock and durables to transfer recipient house- holds, who show large and significant increases in these outcomes. Note, however, that the changes in asset holdings are not jointly significant in the SUR analysis." Haushofer, Reisinger and Shapiro 2015, Pg. 21

• 239

  "Fifth, it is possible that losing a lottery is uniquely disappointing for households; while our analysis of changes in village mean wealth holds constant whether or not (and how many) comparison households won a lottery, losing the lottery may be differentially disappointing depending on the average transfer magnitude of recipient households. Thus, we might expect weaker negative externalities for changes in relative income that are not windfalls. Finally, we point out that GiveDirectly has now moved to a model in which all eligible households in a village receive transfers, rather than only a subset. Together, these considerations suggest that the negative psychological externalities of cash transfers we report here do not detract from the overall positive effects of GiveDirectly’s model, or cash transfers as a whole." Haushofer, Reisinger and Shapiro 2015, Pgs. 22-23

• 240

  “On average, households were surveyed 4.3 months after receiving their last transfer.” Haushofer and Shapiro 2013, Pg. 19

• 241

  "The paper makes three further contributions. First, we take care to distinguish different facets of psychological wellbeing. In particular, psychologists have long distinguished between affective and cognitive components of psychological wellbeing (Diener 2000; Veenhoven 1984), with the former referring to experiences of positive vs. negative affect, such as happiness or sadness, and the latter referring to overall evaluations of one’s life. The justification for this distinction is mainly theoretical, although in factor analysis of survey questions on subjective wellbeing, negative affect, positive affect, and life evaluation emerge as distinct factors (Beiser 1974); in addition, measures of affective vs. cognitive wellbeing have different correlates (e.g. income vs. health, respectively; Kahneman and Deaton 2010). We find relative income effects on life satisfaction, but not on happiness or other psychological variables, suggesting that relative income affects the cognitive, but not the affective component of psychological wellbeing." Haushofer, Reisinger and Shapiro 2015, Pgs. 3-4

• 242

  “On average, households were surveyed 4.3 months after receiving their last transfer.” Haushofer and Shapiro 2013, Pg. 19

• 243

  Aker et al. 2011

• 244

  "Excluding the cost of the mobile phones, the per-recipient cost of the zap intervention falls to $8.80 per recipient. Thus, while the initial costs of the zap program were significantly higher, variable costs were 30 percent higher in the manual cash distribution villages." Aker et al. 2011, Pg 12.

• 245

  Aker et al. 2011, Pg 10.

• 246

  Aker et al. 2011, Tables 4 and 5.

• 247 Fiszbein and Schady 2009.
• 248

  Lagarde, Haines, and Palmer. 2009

• 249

  Haushofer and Shapiro 2013 Policy Brief

• 250

  Blattman, Fiala, and Martinez 2013 and Blattman et al 2013.

• 251

  The file is available here.

  The file is broken into three worksheets. "Main set of RCTs" includes the recent studies that have most influenced our views about cash transfers. This sheet primarily consists of studies that clearly contained evidence of: 1) propensity to invest cash transfers; 2) propensity to spend cash transfers on alcohol, tobacco, or other "temptation goods; 3) recipients' returns on investment; 4) hostility or resentment from cash transfers; 5) effects on inflation or village economies, or other economic effects on non-recipients; 6) differing effects between UCTs and CCTs.

  “Useful non-RCTs and comments” includes relevant non-randomized studies, blog posts or commentary.

  “Other results from Google Scholar” contains information from other recent studies of cash transfers that did not strongly affect our overall views. Most of these studies fall into one of a few categories:

  • non-randomized
  • re-analyses of existing data that focus on various potential secondary benefits or costs of cash transfers. There is widely accessible data relevant to some of the biggest public cash transfer programs, leading researchers to test for effects on a very large number of outcomes that were not pre-registered. For example, we have recently seen studies of Progresa/Oportunidades's effects on elderly mortality and child development. We believe that this type of study is more likely to be affected by publication bias/data mining, so we have not carefully reviewed them.
  • studies of CCTs whose results we would not expect to hold for UCTs (primarily studies that report outcomes that are directly related to the conditions placed on recipients).

• 252
  • We examined the most recent paper on the WINGS program (Blattman et al 2015), so we did not review a prior update on the WINGS program that was published in 2014. We did not make changes to the page based on an additional analysis of WINGS on intimate partner violence (Green et al 2015) or an additional analysis of YOP on various outcomes that emphasized findings on the effect of cash transfers on educational expenditures (Calderone 2014) after examining their abstracts.
  • "Intimate partner violence is widespread and represents an obstacle to human freedom and a significant public health concern. Poverty alleviation programs and efforts to economically “empower” women have become popular policy options, but theory and empirical evidence are mixed on the relationship between women's empowerment and the experience of violence. We study the effects of a successful poverty alleviation program on women's empowerment and intimate partner relations and violence from 2009 to 2011. In the first experiment, a cluster-randomized superiority trial, 15 marginalized people (86% women) were identified in each of 120 villages (n = 1800) in Gulu and Kitgum districts in Uganda. Half of villages were randomly assigned via public lottery to immediate treatment: five days of business training, $150, and supervision and advising. We examine intent-to-treat estimates of program impact and heterogeneity in treatment effects by initial quality of partner relations. 16 months after the initial grants, the program doubled business ownership and incomes (p < 0.01); we show that the effect on monthly income, however, is moderated by initial quality of intimate partner relations. We also find small increases in marital control (p < 0.05), self-reported autonomy (p < 0.10), and quality of partner relations (p < 0.01), but essentially no change in intimate partner violence. In a second experiment, we study the impact of a low-cost attempt to include household partners (often husbands) in the process. Participants from the 60 waitlist villages (n = 904) were randomly assigned to participate in the program as individuals or with a household partner. We observe small, non-significant decreases in abuse and marital control and large increases in the quality of relationships (p < 0.05), but no effects on women's attitudes toward gender norms and a non-significant reduction in autonomy. Involving men and changing framing to promote more inclusive programming can improve relationships, but may not change gender attitudes or increase business success. Increasing women's earnings has no effect on intimate partner violence." Green et al 2015, Abstract
  • We do not quote from Calderone 2014, because it is a preliminary paper and the author has requested that it not be cited.

• 253
  • “On average, household lose 70% of their land and receive compensation payments that are about 5 times the value of annual consumption expenditure.” Harris 2015, Abstract
  • The treatment group: “Households in the treatment group are formally defined as those that report having had any of their land expropriated between rounds.9 But what does it mean for households to be in the treatment group? Fundamentally, the intervention has two related components: 1) households lose their farmland and 2) they receive a cash payment that is a function of how much land was taken.” Harris 2015, Pg. 6
  • The control group: “A group of households that did not lose land were selected from within the same administrative area to serve as a comparison group.” Harris 2015, Pg. 2
  • The sample: “We planned to survey 300 households drawn from 19 sub-villages in one Kebele (the smallest administrative unit in Ethiopia) in which the expropriation was to occur. The sample was restricted to households living in the Kebele at the time of the survey. Together with local officials we identified treated and control households from the Kebele administrator’s household list. 15 households were randomly sampled from each of 16 sub-villages where the treatment status was common across the village. In two villages which contained a mix of treatment and control households we randomly sampled 30 households. One village of the 19 was excluded from the sample because their land had been taken in previous years. During the analysis of the baseline data it became clear that the official’s assessment of the household’s treatment status did not coincide with the household’s own assessment. At the end-line this discrepancy was confirmed: the treatment status was correctly identified by officials for 72% of the sample. There are three main reasons for this: 1) the size of the factory project area was reduced between rounds, 2) an additional area of land was expropriated to expand the town and 3) any random errors on the part of local officials who did not know exactly which households would lose land.”

• 254
  • "One was an 8-week program of group cognitive behavior therapy (CBT) called the STYL program, for Sustainable Transformation of Youth in Liberia. We assigned offers by lottery. Following the therapy, we held a second lottery for an unconditional grant of $200—about three months wages." Blattman, Jamison and Sheridan 2015, Pg. 1
  • "Experimentally, subjects either received therapy, cash, therapy then cash, or neither." Blattman, Jamison and Sheridan 2015, Pg. 1
  • "To investigate, we recruited 999 of the highest-risk men in Liberia’s capital, generally aged 18 to 35. Most were engaged in part-time theft and drug dealing, and regularly had violent confrontations with each other, community members, and police." Blattman, Jamison and Sheridan 2015, Pg. 1

• 255
  • “This report describes the impacts of the winter cash transfer program run by UNHCR and partners from November 2013 to April 2014. The program gave $575 USD via ATM cards to 87,700 registered Syrian refugees in Lebanon with the objective of keeping people warm and dry during cold winter months.” Emergency Economies 2014, Pg. 6
  • ”Fourth, the study rigorously estimates the impacts of cash when $575 was delivered per household over the course of five months” Emergency Economies 2014, Pg. 36
  • "For the impact analysis of the winterization cash transfer program, the Research Team uses a Regression Discontinuity design that exploits the targeting approach of the cash assistance program itself. Cash was given at high altitudes to target assistance for those living in the coldest areas during the winter months.25 Households did not know beforehand that there would be an altitude eligibility cutoff. When the eligibility cutoff was set at 500 meters, households residing at, for example, 501 meters were included, while households residing at, for instance, 499 meters were not." Emergency Economies 2014, Pg. 15

• 256
  • "Empowering young women with cash transfers: findings from a pilot study" GiveDirectly, Final report Nike girls study, Pg. 3
  • "Randomly assigned girls living in 18 villages to control group, 9 villages to $1,000 treatment group, and 9 villages $500 treatment group" GiveDirectly, Final report Nike girls study, Pg. 3
  • "Enrolled 77 girls in the GiveDirectly program, including provision of a mobile phone, and successfully initiated transfers to 76 girls via M-Pesa" GiveDirectly, Final report Nike girls study, Pg. 3

• 257
  • "Randomly assigned girls living in 18 villages to control group, 9 villages to $1,000 treatment group, and 9 villages $500 treatment group" GiveDirectly, Final report Nike girls study, Pg. 3
  • "Enrolled 77 girls in the GiveDirectly program, including provision of a mobile phone, and successfully initiated transfers to 76 girls via M-Pesa" GiveDirectly, Final report Nike girls study, Pg. 3
  • GiveDirectly provides transfers to adult heads of household, while this pilot study targeted young women.
    • "The table below presents key process metrics, alongside data from GiveDirectly's standard UCT program, which provides $1,000 cash grants to adult heads of household in rural Kenya." GiveDirectly, Final report Nike girls study, Pg. 4
    • "Enrolled 77 girls in the GiveDirectly program, including provision of a mobile phone, and successfully initiated transfers to 76 girls via M-Pesa" GiveDirectly, Final report Nike girls study, Pg. 3
  • The pilot study found mostly similar results to GiveDirectly's: "(2) Both girls and adult recipients make responsible investments in housing, food, and livestock, while girls additionally prioritize health and education." GiveDirectly, Final report Nike girls study, Pg. 5
  • Adverse events were rare: "(5) Adverse events amongst recipients are extremely infrequent and in line with adult recipient data, though further qualitative investigation would help to explain case of harm." GiveDirectly, Final report Nike girls study, Pg. 10
  • The study did not report an analysis of returns on investment. Recipients made investments in human capital and physical capital: "Data from the evaluation suggest that UCTs to girls stimulate investment in human capital (education and sexual health), without sacrificing physical capital investments made by older peers (livestock, housing, household items). We find 0.5 year more educational attainment after 1 year, equivalent to 50% of treated girls re-enrolling for the year, and significantly lower rates of STIs." GiveDirectly, Final report Nike girls study, Pg. 2

• 258

  We de-prioritized looking at (a) studies comparing cash to food, (b) studies primarily reporting the effect of cash transfers on maternal and child health outcomes, educational outcomes and/or health intervention uptake outcomes, (c) studies examining alternative interventions (e.g. CCTs for communities involving local councils allocating money to projects based on community input or early childhood development programs making use of the infrastructure/networks established for a cash transfer program), (d) a study of a cash transfer and life skills intervention in San Francisco, California, (e) Google scholar search results that displayed a citation rather than a link to the study itself, (f) editorials on cash transfers, and (g) studies unrelated to cash transfers (e.g. "Do Consumers Pay More Using Debit Cards than Cash? An Experiment").

• 259

  The titles of the 5 studies were:

  • Does the Benefits Schedule of Cash Assistance Programs Affect Impulse Buying? Evidence from a Natural Experiment in Peru
  • Girl Power: Cash Transfers and Adolescent Welfare. Evidence from Cluster-Randomized Experiment in Malawi
  • Community-Based Conditional Cash Transfers in Tanzania: Results from a Randomized Trial
  • Cash Transfer Programme, Productive Activities and Labour Supply: Evidence from a Randomised Experiment in Kenya
  • Households' investments in durable and productive assets in Niger: quasi-experimental evidences from a cash transfer project

  %of the studies (White and Basu 2014) as warranting further investigation (based on a cursory look, none of the other studies reported negative effects). White and Basu 2014, which examined the effect of change in payment schedule for a cash transfer program in Peru on expenditures on temptation goods, did not substantively change our view because it did not, in our view, find meaningfully negative effects (see following footnote for details).

  • White and Basu 2014 found an absolute increase of 0.11-0.17 percentage points in the share of total household expenditures spent on alcohol (from an average of 0.2%) associated with a change in the payment schedule for Peru’s conditional cash transfer program from once a month to once every two months. It doesn’t seem particularly worrisome tha a few more tenths of a percent of their transfer on alcohol when the payment schedule for the transfer changed from once a month to once every two months (even though the relative increase is large).
  • ”A critique of cash assistance programs is that beneficiaries may spend the money on “temptation goods” such as alcohol and tobacco. We exploit a change in the payment sect

• 260
  • White and Basu 2014 found an absolute increase of 0.11-0.17 percentage points in the share of total household expenditures spent on alcohol (from an average of 0.2%) associated with a change in the payment schedule for Peru’s conditional cash transfer program from once a month to once every two months. It doesn’t seem particularly worrisome that cash transfer recipients spent a few more tenths of a percent of their transfer on alcohol when the payment schedule for the transfer changed from once a month to once every two months (even though the relative increase is large).
  • ”A critique of cash assistance programs is that beneficiaries may spend the money on “temptation goods” such as alcohol and tobacco. We exploit a change in the payment schedule of Peru’s conditional cash transfer program to identify the impact of benefit receipt frequency on the purchase of temptation goods. We use annual household data among cross-sectional and panel samples to analyze the effect of the policy change on the share of the household budget devoted to six categories of temptation goods. Using a difference-in-differences estimation approach, we find that larger, less frequent payments increased the expenditure share of alcohol by 55-80% and sweets by 10-40%. Our study suggests that less frequent benefits scheduling may lead cash recipients to make certain types of temptation purchases.” White and Basu 2014, Abstract
  • "Starting in January 2010, the payment schedule in the Juntos CCT program in Peru changed from once a month to once every two months. The total annual payment did not change." White and Basu 2014, Pg. 3
  • Cross-section: 0.0011 (SE: 0.0004). Panel: 0.0017 (0.0009). Panel A, Table 3, White and Basu 2014, Pg. 22
  • "The results from Equation 1 and Equation 2 are presented in Table 3. Estimates of the variable of interest, Tit ×Postt, are displayed for each outcome by temptation expenditure category. In Panel A of Table 3, we analyze the impact on expenditure shares. The coefficients represent the change in the share of expenditures spent on each given category of expenditures. Using the cross-sectional sample, we find that the decreased frequency of payments increased the budget share spent on alcohol and decreased the budget share spent on soft drinks and commercially prepared food. The absolute changes in expenditure shares are small. In Figure 2, we quantify the magnitude of the policy’s impacts by calculating the percentage change in each dependent variable. The increase in alcohol use amounts to 55%, and the decrease in soft drinks and prepared food are 12% and 20%, respectively. Using the panel sample, we find that the decreased frequency of payments marginally increased alcohol expenditure shares by 77%, and significantly increased expenditures on alcohol shares by 102% and sweets shares by 41%." White and Basu 2014, Pg. 10
  • 0.0011/0.55 = 0.002. 0.0017/0.77 = ~0.002. “The percentage change is calculated as the effect size divided by the mean of the dependent” White and Basu 2014, Pg. 23

• 261
  • Harris 2015 found little change in chat or alcohol expenditure: "Finally, it does not appear that households are squandering their cash payments on alcohol or chat (a popular drug in the area); there is no change in chat or alcohol consumption for households that lost their land nor is there an any change for households that received larger payments.17" Harris 2015, Pg. 16
  • “This supposedly undisciplined, lawless group of men largely invested and saved an unconditional grant. Little was spent on temptation goods. This example joins a body of work showing that people seldom ‘waste’ cash (Evans and Popova, 2014).” Blattman, Jamison and Sheridan 2015, Pg. 33
  • Blattman, Jamison and Sheridan 2015 did find an increase of 7.5 percentage points from a baseline of 20% in “usually takes hard drugs” at 12-13 months (95% CI: 1.6% to 13.4%). The paper doesn’t discuss this increase. The study found no evidence of an increase in “Usually uses marijuana.” (Table D.4: Program impacts on Attitudes and Drug Use, Blattman, Jamison and Sheridan 2015, Pg. 31). This population seems at much higher risk of drug abuse than the population targeted by GiveDirectly ("The study recruited 999 young men aged 18 to 35 in five mixed-income areas of Monrovia, focusing on the homeless, men involved in drugs and crime, and poorly reintegrated ex-combatants." Blattman, Jamison and Sheridan 2015, Pg. 5).
  • ”The study found no evidence of a number of hypothesized negative consequences of cash assistance. For instance, there was no evidence of beneficiaries spending cash assistance irresponsibly or meaningfully reducing labor supply. The research did not find that cash assistance exacerbates corruption and exploitation.” Emergency Economies 2014, Pg. 7

• 262
  • "The transfer was conditional on the designated caregiver attending bimonthly health educational workshops and children under five going to regular preventive healthcare visits that included growth monitoring. Health services were free and delivered by private health providers contracted by RPS [the Nicaraguan CCT program]." Barham, Macours and Maluccio 2013, Pg. 468
  • We do not quote from Gilligan and Roy 2014, because it is a preliminary paper and the authors have requested that it not be cited.