Published: December 2012
Published: December 2012
There are three types of cash transfer programs that have been studied:
The program conducted by GiveDirectly, our #2-rated charity, 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 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.
Cash transfers are potentially attractive for individual donors because they allow the recipients of charity to choose how to spend funds allocated for them. Provided that local markets can supply it, if the recipients feel that they need food, they can use their cash to purchase it; if they need medical care, they can buy it; if they have a business, they can invest in it. As we wrote in 2009:
Why do cash handouts seem to be so rare in the charity world? Perhaps it’s because extensive experience and study have shown this approach to be inferior to others. Or perhaps it has more to do with the fact that giving out cash fundamentally puts the people, rather than the charity, in control.
Below is a full list of the cash transfer programs evaluated by randomized controlled trials (RCTs) that we have found.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.
|Program||CCT, UCT, Business grant?||Conditions||Size and frequency||Key Findings|
|Oportunidades (formerly PROGRESA) (1997-), Mexico3||CCT||Health: checkups for all in household, lectures for 15+; Education: 80% attendance, complete middle school, compete grade 12 before 22.4||20% of PCE;5 bimonthly6||10-20% increase in food consumption (more); 6% increase in long-term consumption (more)|
|Programa de Asignacion Familiar (PRAF)(1998- ), Honduras7||CCT||Health visits and 85% school enrollment8||9% of PCE;9 every 6 months10||N/A (all outcomes measured were conditioned outcomes)|
|Red De Proteccion Social (RPS) (2000-), Nicaragua11||CCT||Health: workshops, regular health care visits, up-to-date vaccinations, adequate weight gain; Education: enrollment, 85% attendance, grade promotion.12||27% of PCE;13 bimonthly14||~15% increase in household expenditures; ~25% increase in food expenditures; no increase in investment (more)|
|Atencion a Crisis (2005), Nicaragua15||CCT||Education: enrollment, 85% attendance; occupational training course; business grant plan.16||18% of PCE;17 bimonthly18||~30% higher food consumption; more use of health services; improved self-reported health but unimproved on anthropometric measures (more)|
|Bono de Desarrollo Humano (2003-), Equador19||CCT but not monitored||No monitoring. Without being monitored: Health check-ups (0-5), Education: enrollment, 90% attendance.20||10% of PCE;21 monthly22||Mixed impact on school enrollment, child labor and cognitive development (more)|
|Programa Apoyo Alimentario, Mexico23||CCT but not monitored||No monitored conditions24||11.5% of pre-transfer consumption;25 bimonthly26||Slight improvements in weight for in-kind transfers (not for cash); slight decrease in self-reported sickness for both (more)|
|Zomba Cash Transfer Program, Malawi (2008-)27||CCT & UCT||Unconditional group and conditional group (80% or better school attendance)28||15% of household consumption;29 monthly30||Improved school attendance & performance (more for conditional transfers); reduced psychological distress during but not after transfer period|
|Cash Transfer for Orphans and Vulnerable Children (CT-OVC), Kenya (2007-)31||UCT||Unconditional||21% of household spending;32 monthly33||Increase food consumption by 17% (more); may increase school enrollment amongst older students|
|Micro-enterprise RCT, Sri Lanka (2005)34||Grant||Unconditional35||32.5% of annual profits;36 once37||>60% annual return on investment via increased business profits for two years, continuing for at least five years for men but not women, with no clear differences between cash and in-kind grants (more)|
|Micro-enterprise RCT, Ghana (2009)38||Grant||Unconditional||12% of annual profits;39 once40||No statistically significant impact on business profits for cash grants; ~20% monthly returns for in-kind grants (more)|
|Micro-enterprise RCT, Mexico (2005-2006)41||Grant||Unconditional42||4% of annual profits;43 once44||Returns of 28 to 46% per month based on impact on business profits, with indistinguishable differences between cash and in-kind grants (more)|
A more detailed version of this table is available here (XLS).
GiveDirectly's program is substantially different from the cash transfer programs that have previously been studied. Accordingly, it is not clear that evidence from 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:
Despite the questions about the applicability of the evidence from other cash transfer programs to GiveDirectly's programs, we review the evidence about the use of cash transfers from academic studies 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"45 - such as milk, meat, fruits, vegetables, and eggs.46
Across the four randomized control trials where it is measured in comparable terms, increases in spending on food makes up more than half of the transfer amount:
Cash transfers could be used for alcohol or tobacco, which may have adverse effects.
The three randomized controlled trials of cash transfers that report spending on alcohol or tobacco do not find large increases due to cash transfers:
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).56
Taking into account the three studies and the potential for bias, we would guess that any increases in consumption of alcohol or tobacco due to cash transfers would be small.
We have seen five studies examining the extent to which people invest their cash transfers, leading to longer-term gains:
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.68
Note, though, that the cash transfers by GiveDirectly are both larger and made to poorer individuals than any of the transfers discussed above:
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. Gertler, Martinez, and Rubio-Codina estimate 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.69 This implies, by our calculation, a 1.7% monthly return, and a 21% annual return, on the transfers,70 which further implies a 3.6% monthly, and 42.6% annual, rate of return on investment.71
Using a different method, Gertler, Martinez, and Rubio-Codina estimate 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.72 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.73
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 have received had their children had perfect attendance.74 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.75 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).76 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 $1.60.77
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.
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:
Note that the absolute level of investment in these studies is substantially smaller than our estimate of the level of investments stimulated by GiveDirectly's cash transfers, so the possibility of declining marginal returns to investment would suggest that GiveDirectly recipients may obtain lower average returns on investment than those observed in these studies.
We have not conducted a cost-effectiveness analysis that attempts to quantify the benefits of cash transfers in humanitarian terms. Instead, in comparing cash transfers to the interventions conducted by our two other top charities, we have attempted to monetize some of the benefits of the latter, in particular the “developmental effects” of deworming and bednets. (In the case of the comparison with bednets, for instance, this means quantifying the estimated impact of bednets on later-in-life income of children, through a comparison with the effects of deworming, and then subjectively comparing the cost per life saved with the value of that amount of money as a cash transfer.)
In practice, these calculations are highly sensitive to assumptions, especially regarding:
We guess that in purely programmatic terms, and given our values, bednet distributions are more cost-effective than deworming, which is more cost-effective than cash transfers. However, we think there are plausible values for these assumptions that would permit any ordering of the three programs.
Details of our cost-effectiveness analysis are discussed in a 2012 blog post. The general picture is that deworming appears to be between 2 and 5 times as cost-effective as cash-transfers, in financial terms. We encourage readers who find formal cost-effectiveness analysis important to examine the details of our calculations and assumptions, and to try putting in their own. To the extent that we have intuitive preferences and biases, these could easily be creeping into the assumption- and judgment-call-laden work we’ve done in generating our cost-effectiveness figures, and we’re not entirely confident that the figures themselves are adding substantial information beyond the intuitions we have from examining the details of them.
More, including links to our spreadsheets, at our 2012 discussion of the cost-effectiveness of cash transfers and other interventions.
There are a few potential adverse effects of cash transfers:
Note that there is substantially more evidence suggesting that conditional cash transfer programs lead to reductions in child labor,94 which may help explain the gap between transfer sizes and observed increases in consumption.95
There has been one RCT comparing physical cash transfers with electronic transfers to a recipient's cell phone.96 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.97 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).98 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.99 The study did not find any adverse effects of using cell phone transfers relative to handing out physical cash.
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 review100 and a Cochrane review.101 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 review.
See Bono de Desarrollo Humano (BDH) and Programa Apoyo Alimentario in the programs table below.
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 et al. 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.
Fiszbein and Schady 2009, Pg 268.
Transfers represent 20% of baseline per capita expenditures (a measure of consumption) amongst beneficiaries.
Fiszbein and Schady 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.
Fiszbein and Schady 2009, Pg 212.
Fiszbein and Schady 2009, Pg 264
Fiszbein and Schady 2009, Pg 272.
Fiszbein and Schady 2009, Pg 270.
Fiszbein and Schady 2009, Pg 258.
"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 Gonzalez-Cossio 2008, Pgs 8-9.
Skoufias, Unar, and Gonzalez-Cossio 2008, Pg 15.
Baird, McIntosh, and Ozler 2011.
“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.
“The cash payments take place monthly at centrally located and well-known places, such as churches and schools.” Baird et al. 2009, Pg 13.
The Kenya CT-OVC Evaluation Team 2012.
The Kenya CT-OVC Evaluation Team 2012 A. “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.” Pg 14. 300/1442 = 20.8%
de Mel, McKenzie, and Woodruff 2008. “Cash treatments were given without restrictions. Those re- ceiving 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.” Pg 1337.
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%.
“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.
Fafchamps et al. 2011.
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%.
“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.
McKenzie and Woodruff 2008.
“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.
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%
“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.” McKenzie and Woodruff 2008. Pg 466.
Fiszbein and Schady 2009, Pg 16.
"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) show 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 Attanasio (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.
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.
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%.
The Kenya CT-OVC Evaluation Team 2012 A:
Cunha 2011, Pg 22. In particular, as indicated above, food consumption was reported to increase by 94% of the total transfer amount.
Maluccio and Flores 2005, Pg 32. Table 4.5.
Maluccio and Flores 2005, Pg 32.
The Kenya CT-OVC Evaluation Team 2012 A, 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.)
Three possible forms of misreporting would have different effects:
"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 et al. 2012, Pg 2.
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 trans- fers 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.
Gertler, Martinez, and Rubio-Codina, 2012. Pg 189.
Maluccio and Flores 2005. Pg 33.
Kenya CT-OVC Evaluation Team 2012 A. “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.” Pg 23.
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.
de Mel, McKenzie, and Woodruff 2008. “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.” Pg 1337.
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.”
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.
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.
Gertler, Martinez, and Rubio-Codina, 2012. “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 ben- efits. 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).” Pg 179.
“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%
Table 8 reports that the difference between monthly transfer and increase in consumption was:
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.
Gertler, Martinez, and Rubio-Codina, 2012:
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.
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.
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%).
Gertler, Martinez, and Rubio-Codina, 2012. “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.” Pg 187.
Gertler, Martinez, and Rubio-Codina, 2012. Table 10, column 1.
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)
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.
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.
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.
de Mel, McKenzie, and Woodruff 2008. Table V.
de Mel, McKenzie, and Woodruff 2012. Table 3.
Fafchamps et al. 2011.:
McKenzie and Woodruff 2008:
McKenzie and Woodruff 2008. “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.” Pg 479.
McKenzie and Woodruff 2008. “One potential concern is whether the process of trimming com- bined 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.” Pg 476.
"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 Georgi, and Jayachandran 2011, Pg 14-15.
Cunha, de Georgi, and Jayachandran 2011, Table 2, Pg 35.
"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 Georgi, and Jayachandran 2011, Pg 15. However, the authors report only the change in prices for the PAL goods.
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.
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 add: (Pg 122) "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."
Angelucci and De Giorgi 2009, Table 1.
“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 (2008) 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.
The evidence we have seen cannot distinguish between:
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 write, “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) show that the Bono de desarrollo humano program had very large effects on child work among those children most vulnerable to transitioning from school- ing to work. those effects are concentrated in work for pay away from the child’s home. on the other hand, Bdh transfers 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 rps reduced child work by 3–5 percentage points among children aged 7–13 (maluccio and flores 2005). furthermore, the fraction of children who only studied (as opposed to worked and studied, only worked, or neither worked nor studied) increased signifi- cantly (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 petI, 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, conditional on school attendance and participation in special training workshops. petI beneficiaries reduced substantially their probability of working. attanasio et al. (2006), however, find 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); and glewwe and olinto (2004) find no effects 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. potentially, programs of this nature could have positive or negative spillovers for other siblings—pos- itive 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 if parents compensate for the reduction in work of one child by increas- ing the work of other siblings. Barrera-osorio et al. (2008) analyze subsidio Condicionado 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. on the other hand, 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.
Fiszbein and Schady, 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:
Aker et al. 2011.
"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.
Aker et al. 2011, Pg 10.
Aker et al. 2011, Tables 4 and 5.
Lagarde et al. 2009, “The impact of conditional cash transfers on health outcomes and use of health services in low and middle income countries.”