Spillover Effects Literature Review
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A. Studies we have reviewed in detail
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ResultsMethodologyProgram DesignContext
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Paper
Abbreviation
LinkSpillover effect on consumptionSource
Spillover effects on other outcomes
SourceIdentification strategySourceRCT designSource
Sample size for regression underlying main spillover estimate
Source
Duration between transfer and follow-up
SourceMethodological limitationsSourceSize of transferSourceProportion of village treatedSourceEligibility criteriaSourceIs it a GD program?SourceCountrySourceOther Notes
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Haushofer, Miguel, Niehaus & Walker (2018) ("GE study")
GE187%* within village, 1% across villageWithin-village: "...we do find that ineligible households in treatment villages report a marginally significant increase in consumption (USD 170 PPP), 9 percent of the typical transfer value and 7 percent of the control group mean", p.21. Panel B of Table 3 contains the results. Across-village: In column (1) of Table 4, the authors present the across-village spillover effect estimates pooling across households (i.e. across both eligible and ineligible households for both the treated and control groups). They summarise the results as a % of the "mean for households in control villages in low saturation sublocations" in column (5) of Table 4, which is a 1% increase, not statistically significant.
No statistically significant across-village spillover effect on asset ownership or subjective well-being. No statistically significant effect on prices. These nulls are precise. A positive and statistically significant within-village effect on subjective well-being approx. one tenth of a standard deviation in size.
See Table 4, p.24 for the across-village spillover effect on assets. See Table 1 and Table 2, p.20, for the within-village and across-village spillover effects on subjective well-being respectively. "...we also find that ineligible households in treatment villages also report significant increases in subjective well- being of 0.11 SD (p < 0.01)", p.4. See Table 6 on p.26 for effects on prices.
Within-village: compare the consumption of ineligible households in treatment villages with ineligible households in control villages. Across-village: compare consumption across households in high and low saturation sublocations for a given household type (for each combination of eligible or ineligible, and treated or control).
Within-village: See equation (1) on p.15. Across-village: See equation (2) on p.15.
Groups of ~10 villages called 'sublocations' are assigned to low or high saturation (in low saturation sublocations, 1/3 of villages are treated; in high saturation sublocations, 2/3 of villages are treated), and then within sublocations villages are assigned to either treatment or control. All eligible households in the treated villages are assigned to treatment."Treatment assignment is randomized at the village level, and within treatment villages, all households meeting GD’s eligibility requirement receive the unconditional cash transfer. A second level of randomization provides variation in treatment intensity: sublocations, an administrative unit directly above the village level comprising of an average of ten villages, were randomly assigned to high or low saturation status. In high saturation sublocations, two-thirds of villages were assigned to treatment, while in low saturation sublocations, only one-third of villages were assigned to treatment", p.2. "In treatment villages, GD enrolls all households in treatment villages meeting its thatched-roof eligibility criteria (“eligible” households)", p.6.Across-village: 8,237. Within-village: 2,815.
Across-village: See column (7) of Table 4, p.24. Within-village: See column (6) of Table 3, p.23.
10 months on average after final transfer. Final transfer was approximately 8 months after the first transfer.
"...we summarize results on subjective well-being, household assets and expenditure from our first endline survey, conducted on average 10 months after the distribution of the final transfer", p.2. "The cash is transferred in a series of three payments via M-Pesa according to the following schedule: (i) the token transfer of about USD 70 nominal / USD 150 PPP ensures the system is working properly; (ii) two months afterwards, the first lump sum transfer of about USD 415 nominal / USD 860 PPP is distributed; (iii) six months after this, the second and final lump sum transfer of USD 415 nominal / USD 860 PPP is sent", p.7.
Generally very strong study methodologically compared to the rest of the literature, particularly on account of its large sample size and the fact that it directly estimates an across-village as well as a within-village spillover effect. Minor limitation: 1) The authors try to deal with potential bias in the within-village spillover effect estimates caused by the existence of across-village spillover effects (which other within-village estimates in the academic literature suffer from) by controlling for sublocation saturation status in their within-village spillover regressions. If across-village spillover effects only operate within and not across sublocations, this perfectly deals with the problem. However, if across-village spillover effects occur across sublocation boundaries, there will still be some bias (likely of a smaller magnitude) since ineligible households in control villages experience spillovers from other sublocations.N/A
$1000 US (nominal), or $1,870 PPP. Approx 75% of annual expenditure for recipient households.
"The magnitude of the transfers is large, around USD 1,000 (nominal) per household, or about USD 1,870 PPP, roughly 75% of annual expenditure for recipient households", p.2.
33%
"In treatment villages, GD enrolls all households in treatment villages meeting its thatched-roof eligibility criteria (“eligible” households); approximately one-third of all households are eligible", p.6.
Grass-thatched roof
"In treatment villages, GD enrolls all households in treatment villages meeting its thatched-roof eligibility criteria (“eligible” households)", p.6.
Yes
"We conduct a large-scale randomized controlled trial of the unconditional cash transfer pro- gram of the NGO GiveDirectly (GD)", p.2.
Kenya (one county - Siaya, rural Western Kenya)
"This study takes place in Siaya County, Kenya, a rural area in western Kenya bordering Lake Victoria", p.6.
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Haushofer & Shapiro 2018 (3-year follow-up)
HS18http://jeremypshapiro.com/papers/Haushofer_Shapiro_UCT2_2018-01-30_paper_only.pdf-16%***"The point estimates suggest spillover households spend USD 30 PPP less than pure control households, or about 16% based on a pure control mean of USD 188 PPP", p.3. Results are presented in column (5) of Table 7 on p.26.
Negative and significant spillover effects on food security and psychological well-being, and a positive and significant spillover effect on female empowerment, all of which are robust to the authors' approach to dealing with the issue of endogenous control group selection. They find a negative and significant spillover effect on assets, but this is sensitive to the choice of sample used to deal with the endogenous control group selection. When the authors use Lee bounds to deal with the differential attrition rate between the pure control and spillover groups, the lower and upper bound estimates are not both statistically significant for all sample choices (used to deal with endogeneity of control group selection). For assets, revenue and food security it is only for one of the three sample choices that both the lower and upper bound estimates are statistically significant. They also find suggestive evidence of negative spillover effects on the value of productive assets such as livestock, bicycles, motorbikes and appliances.
See Table 7 on p.26 for the spillover effect estimates in the original sample and in the samples used to deal with endogenous control group selection criteria. See Table 8 on p.27 for the spillover effect estimates using Lee bounds to deal with differential attrition.
Compare the consumption of control households in treatment villages to the consumption of households in control villages.
See equation (12) on p.24.
Villages are randomly assigned to treatment and control, and within treatment villages eligible households are randomly assigned to treatment or control (~50% in each). "The research team then identified the 120 villages with the highest proportion of thatched roofs within Rarieda. Sixty villages were randomly chosen to be treatment villages (first stage of randomization)", p.5. "After baseline, the research team randomly chose half of the eligible households to be transfer recipients (second stage of randomization). This process resulted in 503 treatment households and 505 control households in treatment villages at baseline", p.6.830
See column (6) of Table 7 on p.26. This is the size of the original sample.
3 years on average after the first transfer. Transfers were either made monthly for eight months or as one lump-sum payment in a randomly chosen month during the nine month period from the initial visit.
"The results reported here capture the impacts of unconditional cash transfers approximately 3 years after the transfers were sent", p.3. "For monthly transfers, the first installment was transferred on that day, and continued for eight months thereafter; for lump-sum transfers, a month was randomly chosen among the nine months following the date of the initial visit", p.7.
1) For within-village spillover effect estimates to be unbiased, they must assume that across-village spillover effects do not exist. 2) Attrition rates are significantly higher in control villages than treatment villages, including for spillover households specifically, between the first and second endlines (note that no baseline survey exists for control villages). 3) In control villages, households were selected into the sample just before the first endline survey rather than at the baseline. This means the eligibility criterion was applied to them ~1 year after it was applied to the control group. During that year, some households may have upgraded from a thatched to a metal roof and so become ineligible for survey. The pure control group households are a selected sample who did not upgrade to metal roofs during the year between baseline and first endline surveys, and so may not be comparable to households in treatment villages (including control households in treatment villages, i.e. "spillover" households). However, the authors noted that they attempted to correct for this problem by using retrospective surveys, and found that the resulting difference in selection was extremely small. So, this limitation may be less relevant.
"A potential weakness in this analysis is that the thatched-roof selection criterion for participation in the study was applied to households in control villages one year after it was applied to households in treatment villages. As a result, there is endogenous selection into the pure control condition, as some proportion of households in pure control villages are likely to have upgraded to a metal roof over this time period. These households are excluded from endline in the pure control villages", p.19. "...there is a statistically significant difference in attrition levels for households in control villages relative to households in treatment villages from endline 1 to endline 2: 6 percentage points more pure control households were not found at endline 2 relative to either group of households in treatment villages", p.9.
$490 US (nominal) on average. Some receive large transfers ($1525 US PPP), others small ($404 US PPP). Average transfer is $709 US PPP, or ~2 years of per-capita expenditure.
"...the total transfer amount received by these [the large transfer] households was KES 95,200 (USD 1,525 PPP, USD 1,000 nominal). The remaining 366 treatment households constitute the “small” transfer group, and received transfers totaling KES 25,200 (USD 404 PPP, USD 300 nominal) per household", p.5. "GD sent unconditional cash transfers averaging USD 709 PPP, which corresponds to almost two years of per-capita expenditure", p.2. The paper doesn't seem to report the average transfer amount in nominal USD, but given that the small and large transfers are $300 US and $1,000 US nominal, which is equal to $404 and $1,525 in US PPP, then if: 404x + 1525(1-x) = 709, x = 72.8%, then the average nominal transfer = 300(0.728) + 1000(1-0.728) = $490 US.
9%
"An average of 19 percent of households per village were surveyed, and an average of 9 percent received transfers", p.5.
Grass-thatched roof
"A household was considered eligible if it had a thatched roof", p.6.
Yes
"In particular, we studied the economic and psychological impacts of cash transfers provided by the NGO GiveDirectly (GD) in Kenya", p.2.
Kenya (one district - Rarieda)
"GD first identified Rarieda, Kenya, as a study district, based on data from the national census", p.5.
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Haushofer & Shapiro 2016 (9-month follow-up)
HS16https://academic.oup.com/qje/article/131/4/1973/2468874-4%We have taken the results from column (1) in Table III, p.2004 (the regression specification which does not include controls for baseline covariates). When including controls, the effect becomes slightly larger in absolute magnitude and statistically significant at the 10% level (see column (2)). The point estimate in column (1) a $7.77 decrease in monthly non-durable expenditure. From a control group mean of $182 (see column (1) in Table I, p.1992), this is a 4% decrease.
No negative spillover effects on assets, food security or revenue. They find a positive and significant spillover effect on female empowerment. They find a marginally significant effect of cash transfers on non-food prices, and very imprecise nulls on other price variables, in village-level regressions.
See Table III on p.2004 for spillover effect estimates. "We find no significant village-level effects, except for a marginally significant effect on the index of nonfood prices", p.2009 (see Online Appendix Table 149 for results of village-level price regressions).
Compare the consumption of control households in treatment villages to the consumption of households in control villages. The authors also report regressions in which they compare consumption of control households in treatment villages with different treatment intensity (similar to the HRS15 identification strategy, though get different results for economic variables due to different regression specifications (compare equations 1-2 in HRS15 and equation 7 in HS16 online appendix) - see Online Appendix Table 27). They also run village-level regressions comparing treatment to control villages.
See equation (10) on p.2002 for main spillover effect regression specification. See equation (11) on p.2009 for village-level specification.
Villages are randomly assigned to treatment and control, and within treatment villages eligible households are randomly assigned to treatment or control (~50% in each). See source for Haushofer and Shapiro 2018, based on the same RCT.901
See the flow chart on p.1982, which reports that at endline there were 469 spillover households and 432 control households. (Number of observations not reported in main results table, Table 3).
9 months on average after the first transfer. Transfers were either made monthly for eight months or as one lump-sum payment in a randomly chosen month during the nine month period from the initial visit.
"Households received the first transfer an average of 4.8 months after baseline and an average of 9.3 months before endline", p.1984. "The transfer schedule commenced on the first day of the month following the initial visit. For monthly transfers, the first installment was transferred on that day, and continued for eight months thereafter; for lump-sum transfers, a month was randomly chosen among the nine months following the date of the initial visit", p.1984.
1) For within-village spillover effect estimates to be unbiased, they must assume that across-village spillover effects do not exist. 2) In control villages, households were selected into the sample just before the first endline survey rather than at the baseline. This means the eligibility criterion was applied to them ~1 year after it was applied to the control group. During that year, some households may have upgraded from a thatched to a metal roof and so become ineligible for survey. The pure control group households are a selected sample who did not upgrade to metal roofs during the year between baseline and first endline surveys, and so may not be comparable to households in treatment villages (including control households in treatment villages, i.e. "spillover" households). However, the authors noted that they attempted to correct for this problem by using retrospective surveys, and found that the resulting difference in selection was extremely small. So, this limitation may be less relevant.
See source in Haushofer and Shapiro 2018 for the issue of endogenous selection criterion for the control group.
$490 US (nominal) on average. Some receive large transfers ($1525 US PPP), others small ($404 US PPP). Average transfer is $709 US PPP, or ~2 years of per-capita expenditure.
See source for Haushofer and Shapiro 2018, based on the same RCT.9%
See source for Haushofer and Shapiro 2018, based on the same RCT.
Grass-thatched roof
See source for Haushofer and Shapiro 2018, based on the same RCT.
Yes
See source for Haushofer and Shapiro 2018, based on the same RCT.
Kenya (one district - Rarieda)
See source for Haushofer and Shapiro 2018, based on the same RCT.
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McIntosh & Zeitlin 2018MZ18https://www.poverty-action.org/sites/default/files/publications/Benchmarking.pdf
-12% (statistical significance unknown)
This estimate is backed out in this blog post by Ozler: https://blogs.worldbank.org/impactevaluations/most-good-you-can-do-whom. "The final column, which gives the impact sizes on ineligible households, implies that there may have been as much as a ...12% decline in consumption."
Suggestive evidence of negative spillover effects on wealth and dietary diversity, backed out from the ITT and TCE estimates, though statistical significance of those results is unclear.
"The final column, which gives the impact sizes on ineligible households, implies that there may have been as much as a 50% decline in total HH wealth...and about a 7% decline in the dietary diversity score", see Ozler's post: https://blogs.worldbank.org/impactevaluations/most-good-you-can-do-whom.
The authors estimate ITT (intent-to-treat) effects for eligible households by comparing outcomes for eligible households in treated villages to eligible households in control villages. They estimate TCE (total causal effects) by pooling eligible and ineligible households and comparing them between treated and control villages. We can use these two estimates to back out the spillover effect on ineligible households (SNT) (because the TCE is just a weighted average of the ITT and SNT).
See equation (1) on p.17 for ITT identification strategy, and TCE: "using (1) but including the ineligible sample and using weights to reflect the whole village population", p.28. See Ozler's post for description of backing out SNT: https://blogs.worldbank.org/impactevaluations/most-good-you-can-do-whom.
Villages are randomly assigned to GD program (either small or large cash transfer), a nutrition/health program called Gikuriro, or control. All eligible households in treatment villages are assigned to treatment. "74 villages were assigned to the Gikuriro intervention, 74 were assigned to the control group (no intervention), and 100 were assigned to GiveDirectly household grants. The GiveDirectly villages were further split into four transfer amounts, randomized at the village level. Three treatment amount arms, with 22 villages in each, received transfer amounts in a range around the anticipated cost of Gikuriro. A final 34 villages were assigned to the ‘large’ GiveDirectly transfer amount which was selected by GiveDirectly as the amount anticipated to maximize the cost effectiveness of cash", p.13.966
2,710 households in the TCE regressions (see Panel A, column (1) of Table 8, p.49), and 1,744 eligible households in the ITT regressions (see Panel A, column (1) of Table 5, p.46). Therefore there are 2,710-1,744 = 966 ineligible households, for whom the spillover effects are backed out.
12 months between the endline and the start of the GD program. Recipients either received transfers as a sequence of monthly payments or all up-front as one lump-sum payment.
"...the study is only able to measure impacts over the course of the 13 months from baseline to endline, which capture 12 months of on-the-ground implementation for GD", p.9. "We randomized eligible beneficiaries in the household grants arm of the study to three groups designed to measure the effect of frequency: flow transfers divided into a sequence of monthly transfers; lump-sum transfers given all up front; and a choice arm that could decide which of these two modalities they wanted", p.14.
1) For within-village spillover effect estimates to be unbiased, they must assume that across-village spillover effects do not exist. 2) Does not directly estimate spillover effects. Spillover effects can be backed out from the ITT and TCE estimates. However, as a result we have not seen tests of statistical significance of those spillover effects. 3) Study is underpowered to detect spillover effects because few ineligible households are surveyed.
"The authors designed the study so that we could see not only the effects on the targeted beneficiaries of each program, which constituted about one in five residents, on average, of each study village, i.e. the intention-to-treat effect (ITT), but also for the villages as a whole, the so-called total causal effect (TCE). This requires sampling not only households eligible for the intervention(s), but also a random sample of those who are ineligible. Comparing the latter to the pure control group gives us spillover effects on the non-treated (SNT), and a weighted average of the ITT and the SNT is equal to the TCE." "...despite the fact that ineligible population outnumbers the eligible one, there are almost twice as many eligible HHs in the sample, or four per village. The study is underpowered to detect the TCE and the SNT", see https://blogs.worldbank.org/impactevaluations/most-good-you-can-do-whom.
$532 US (nominal)
"The fourth and much larger transfer arm transferred $532", p.5.
11%
"With 11.4 percent of all households being defined as eligible", p.28
Households with a malnourished child/in bottom two quintiles of poverty classification and have an under-5 child/in bottom two quintiles of poverty classification and have a pregnant or lactating mother.
"We therefore used a definition of eligibility tailored to Gikuriro’s stated target population: namely, households that contained malnourished children, or pregnant and lactating mothers...CRS and USAID agreed that the following criteria represent the target population for Gikuriro: Criteria 1. All households in a village with a malnourished child (defined by a threshold value of weight/age) were enrolled. Criteria 2. All households in Ubudehe 1 or 2 with children under the age of 5 (Ubudehe is the Rwandan government household-level poverty classification, with 1 being the poorest, 3 being non-poor, and rural areas containing very few of the wealthiest Ubudehe 4 households). Criteria 3. All households in Ubudehe 1 or 2 with a pregnant or lactating mother. Both implementers agreed to attempt to treat all eligible households that were identified as meeting any of these criteria", p.10.Yes
"The benchmarking household grant program was implemented by GiveDirectly, a US-based nonprofit that specializes in making unconditional household grants via mobile money", p.2.
Rwanda (two districts - Kayonza and Nyabihu)
"The study takes place in Kayonza and Nyabihu, two districts that span the range of economic and health outcomes observed in Rwanda", p.4.Some ineligible households also get treated (treatment rate in the ineligible sample is 8.4%), though this proportion is small and so spillover effects should largely be driven by spillovers rather than capturing direct treatment effects for the ineligible. "the treatment rate in the ineligible sample is 8.4 percent. This means that the large majority of the additional sample included in the TCE analysis only receive impacts through spillover effects to untreated households", p.28.
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Haushofer, Reisinger & Shapiro 2015
HRS15http://www.princeton.edu/haushofer/publications/Haushofer_Reisinger_Shapiro_Inequality_2015.pdf-14%*"Specifically, we find that a USD 100 increase in village mean wealth results in a USD 7.23 decrease in total monthly non-durable consumption, significant at the 10 percent level", p.21. "...the average level of village wealth change (USD 354)", p.18. Multiplying 7.23 by (354/100), we get a US$25.60 decrease. The authors do not seem to report summary statistics on monthly household consumption (e.g. in Table A.1. or Table A.6.4.). We therefore convert this spillover effect estimate to a % of consumption using the mean household monthly non-durable consumption for the control group reported in column (1) of Table 1 in Haushofer and Shapiro 2016, which is $182.
Negative and significant spillover effect on life satisfaction, though the effect is not significant after making adjustment for multiple hypothesis testing, and there are no effects on other psychological outcomes. Negative and significant spillover effects on asset holdings. The authors look at a very large range of other outcome variables too.
"Columns (3) and (4) of Table 1 show that exogenous changes in village mean wealth have a large negative effect on life satisfaction", p.17. "We note, however, that p-values after FWER adjustment are not significant at standard levels. We find no effects of changes in relative wealth on other psychological outcomes", p.18. "...we also observe a decrease in overall asset levels, as reported in columns (3) and (4) of Table A.6.4", p.21.
Identification of spillover effects is more complicated in this paper, and so the estimates are not directly comparable to the within-village spillover effects estimated in the other papers. Treatment villages had different average transfer sizes per household (both because proportion treated varies across treatment villages and transfer sizes vary), and so roughly speaking spillover effects are estimated by comparing households with a given transfer from the program to similar households in villages with a larger average transfer size.
See a detailed description of the methodology with sources here: https://www.givewell.org/international/technical/programs/cash-transfers#footnote232_2all1rs
Villages are randomly assigned to treatment and control, and within treatment villages eligible households are randomly assigned to treatment or control (~50% in each). See source for Haushofer and Shapiro 2018, based on the same RCT.939
See column 4 of Table A.6.3, p.56.
They have data across the 15 months of the study between the initial visit and endline.
"We calculate...from transfers occurring in overlapping subsets of the period: the 1 month before endline, the 2 months before endline, etc., up through the full 15 months before endline", p.12. "In the case of monthly transfers, the first installment was transferred on the first of the month following the initial visit, and continued for eight months thereafter. In the case of lump-sum transfers, a month was randomly chosen among the nine months following the date of the initial visit", p.5.
1) For within-village spillover effect estimates to be unbiased, they must assume that across-village spillover effects do not exist. 2) Results for economic variables seem to be very different to the results outlined in HS16 using a similar identification strategy.
See Online Appendix Table 27 in Haushofer and Shapiro 2016 for comparison.
$490 US (nominal) on average. Some receive large transfers ($1525 US PPP), others small ($404 US PPP). Average transfer is $709 US PPP, or ~2 years of per-capita expenditure.
See source for Haushofer and Shapiro 2018, based on the same RCT.9%
See source for Haushofer and Shapiro 2018, based on the same RCT.
Grass-thatched roof
See source for Haushofer and Shapiro 2018, based on the same RCT.
Yes
See source for Haushofer and Shapiro 2018, based on the same RCT.
Kenya (one district - Rarieda)
See source for Haushofer and Shapiro 2018, based on the same RCT.
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B. Studies we have reviewed in less detail
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ResultsMethodologyProgram designContext
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Spillover effectsSourceRCT designSource
Duration between transfer and follow-up
SourceSize of transferSourceIs it a GD program?SourceCountrySourceOther Notes
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Baird, DeHoop & Ozler 2013
BDO13http://jhr.uwpress.org/content/48/2/370.shortNegative and significant spillover effect on psychological distress one year after the program began (6.4ppt higher psychological distress). They estimate the spillover effects by comparing untreated schoolgirls in treatment villages to schoolgirls in the control villages. "The first column of Table 8 shows that untreated girls in treatment EAs are significantly more likely to suffer from psychological distress than the control group during the intervention period. Psychological distress among this group is 6.4 percentage points higher than in the control group, statistically significant at the 95 percent confidence level", p.394. Enumeration areas (which consist of several villages) are randomly assigned to treatment (two treatment groups - one receive conditional cash transfers, the other unconditional) or control. Within treatment EAs, schoolgirls are randomly assigned to treatment or control. A randomly selected percentage of schoolgirls in each treatment enumeration area are given cash transfers."Treatment status was assigned at the EA level and the sample of 176 EAs was randomly divided into two equally sized groups: treatment and control." "The 88 treatment EAs were then randomly assigned to one of three groups to determine the treatment status of baseline schoolgirls: in 46 EAs baseline schoolgirls received transfer offers conditional on regular school attendance (CCT arm), while in 27 EAs they received offers for unconditional cash transfers (UCT arm). In the remaining 15 EAs no baseline schoolgirls received any transfer offers. To measure potential spillover effects of the program, a randomly selected percentage of baseline schoolgirls in each treatment EA were randomly chosen to participate in the cash transfer program", p.377.Follow-up one and two years after baseline"The data used in this paper were collected in three household survey rounds. Baseline data (Round 1) were collected between October 2007 and January 2008, before the offers to participate in the program took place. First followup data collection (Round 2) was conducted approximately 12 months later — between October 2008 and February 2009. The second followup (Round 3) data collection was conducted between February and June 2010 —after the completion of the two-year intervention at the end of 2009 to examine the final impacts of the program. The intervention period coincided with the 2008 and 2009 school years in Malawi", p.379.Between $4-$10 US per month"Transfer amounts to the parents were varied randomly across EAs between $4, $6, $8, and $10 per month", p.377.NoMalawi (one district - Zomba)"Malawi, the setting for this research project", "Zomba District in the Southern region was chosen as the site for this study", p.376.School dropouts in all treatment and control enumeration areas receive conditional cash transfers. "In the 88 treatment EAs, all baseline dropouts were offered conditional cash transfers", p.376.
14
Filmer, Friedman, Kandpal & Onishi 2018
FFKO18http://documents.worldbank.org/curated/en/989031522077749796/pdf/WPS8377.pdfNegative and significant spillover effect on child growth (a 12 ppt. increase in child-stunting rates and a 0.4 standard deviation decrease in height-for-age z score for non-beneficiaries). Main focus of the paper is on price effects - they find that cash transfers significantly increase prices of protein-rich perishable foods, which they believe explains the effect on child stunting for non-beneficiaries (a 9% increase in aggregate income in the average village leading to a 6-8% increase in prices of protein-rich perishable foods). There is no price effect on storable and easily traded food goods. To identify the spillover effects they compare ineligible households (who nonetheless have children) between treatment and control villages. "The cash influx did not affect the prices of storable and easily traded food goods but increased the local prices of protein-rich perishable foods by 6 to 8 percent. This rise is the result of a 9 percent increase in aggregate income in the average village. Program beneficiary households were largely protected by the increase in household income; however, these price increases generated significant indirect effects on non-beneficiaries’ welfare. Most notable among such indirect effects is a 12-percentage point increase in child stunting rates (relative to a control mean of 32 percent) and a 0.4 standard deviation decrease in the height-for-age z-scores of nonbeneficiaries", p.5. "...we estimate indirect effects on non-beneficiaries using the village randomized evaluation of Pantawid to compare households above the program eligibility threshold (and therefore ineligible) in treated and control villages", p.2.Villages are assigned to treatment or control. All eligible households receive the cash transfer (eligibility criterion is that household has to be below the provincial poverty line and have at least one child aged 0-14 or a pregnant mother). The cash transfer is conditional on household investments in child education and health, and the use of maternal health services."A total of 130 villages in the eight municipalities were then randomly assigned to treatment or control status with equal probability", p.9. "Eligible households have a proxy means test score below the provincial poverty line and contain children aged 0 to 14 years or a pregnant woman at time of the assessment", p.9. "Poor households with children aged 0 to 14 or pregnant women receive a lump sum health grant of PhP 500 (about USD 11) per household per month if (i) all children under the age of five attend growth monitoring visits at the local health center; (ii) pregnant women seek regular antenatal care; (iii) school-aged children (6 to 14 years old) accept school-based deworming; and (iv) a household member attends monthly health and nutrition workshops", p.9.30-31 months after the program"A follow-up survey was conducted in October and November 2011, allowing a program exposure period of 30 to 31 months", p.9.$11-32 US per month (as a health or education grant), depending on number of eligible children and compliance with the program. Expected transfer size is about 23% of per capita beneficiary consumption.
"These households receive a combination of health and education grants every two months ranging from PhP 500 to PhP 1,400 (approximately 11 USD to 32 USD) per household per month, depending on their number of eligible children and compliance with program conditions. The expected transfer size equaled approximately 23 percent of per capita beneficiary consumption", p.9.
No - Pantawid Pamilya Pilipino Program."randomized evaluation of a large conditional cash transfer program in the Philippines, Pantawid Pamilya Pilipino Program", p.25.Philippines (eight selected municipalities across four provinces)"This paper...using the randomized evaluation of a large conditional cash transfer program in the Philippines, Pantawid Pamilya Pilipino Program", p.25. "A village-randomized evaluation, stratified by eight purposively-selected municipalities in four provinces", p.9.
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Angelucci & DeGiorgi 2009AD09https://files.givewell.org/files/DWDA%202009/Cash%20Transfers/Angelucci%20De%20Giorgi.pdfPositive and significant spillover effects on consumption. Food consumption for ineligibles in treatment villages increases about 10% per month per adult equivalent, which is about half the size of the effect for those eligible for the program. They identify effects by comparing ineligible households in treated and control villages. They also find that ineligible households borrow more (in informal loans), receive more transfers, and to a small extent reduce their stock of grains and animals at the start of the program. They believe the positive effects operate through informal risk sharing networks in these villages. "A comparison of ineligible households’ consumption, loans, and transfers in treatment and control villages enables us to identify the indirect effect of the program on these outcomes", p.3. "If villagers share risk, Progresa will cause an increase in consumption, loans, and transfers for ineligible families. Consistent with those predictions, food consumption for the ineligibles in treated villages increases by about 10% per month per adult equivalent in May and November 1999. This effect is roughly 50% of the average increase in food consumption for eligible adults since November 1998... Ineligible households in treatment villages consume more by borrowing more money (mainly from family and friends), by receiving more transfers, and, to a small extent, by reducing their stock of grains and animals at the beginning of the program", p.3.Villages are assigned to treatment or control. All eligible households receive the cash transfer. The cash transfer is conditional on family visits to health centres, women's participation in informal workshops on health and nutrition issues, and verification that children attended classes at least 85% of the time. The eligibility criterion is that households are classified as poor based on an assessment of their permanent income using census data. About half of households in the study villages are eligible. "The experimental data for the evaluation of Progresa contain information on households from 506 poor rural villages in seven different states. Because of the program’s geographic phase-in, 186 villages are randomized out and receive the treatment only at the end of 1999. Program eligibility depends on poverty status, and households are classified as being eligible or ineligible according to an assessment of their permanent income from information collected in the September 1997 census of localities...52% of households were classified as eligible in 1997", p.6. "The grants, paid bimonthly, are conditional upon family visits to health centers, women’s participation in informal workshops on health and nutrition issues, and verification that children attended classes at least 85% of the time", p.5.Program began one semester before November 1998, and they have follow-up data in November 1998, May 1999 and November 1999, so up to a little over one year after program began"After the start of the program, all residents of control and treatment villages are first interviewed in November 1998 - about a semester after the beginning of the payments - and then in May and November 1999. This provides information from three different points in time after the beginning of the program", p.7.On average ~200 pesos, which is ~23% and 16% of the average food consumption per adult equivalent in poor and non-poor households in control villages. At the time the exchange rate was approximately 10 pesos to 1 USD."The actual monthly grants up to November 1999 are sizeable, averaging 200 pesos per household, or 32.5 pesos per adult equivalent. This is about 23% and 16% of the average food consumption per adult equivalent for the poor and non-poor in control villages (which are respectively 140 and 200 pesos)", "The exchange rate is approximately 10 pesos for 1 US dollar", p.6.No - Oportunidades (formerly Progresa) program."This paper estimates the indirect effects of the flagship Mexican welfare program, Progresa", p.2.Mexico (across seven states)"Progresa (currently re-named Oportunidades) is an ongoing Mexican poverty alleviation program that targets poor households, providing grants to improve education, health, and nutrition", p.5. "The experimental data for the evaluation of Progresa contain information on households from 506 poor rural villages in seven different states", p.6.
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