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ABSTRACT
Conditional Cash Transfer (CCT) programmes are important anti-poverty programmes. There is relatively little evidence, however, of ongoing effectiveness several years after they have begun. Such evidence is particularly relevant for policymakers because programme effects may become larger or smaller over time. We analyse whether children exposed since birth to a CCT in El Salvador have better schooling outcomes at initial school ages. The results demonstrate that exposure significantly increased school enrolment and attainment for five-year-olds in preschool. The pattern of impacts suggests continued programme exposure might be improving primary school readiness or shifting norms around child investment.
Supplementary material
The supplemental data for this article can be accessed here
Disclosure statement
No potential conflict of interest was reported by the authors.
Notes
1. Calculations based on IDB Sociometro, available at https://www.iadb.org/en/research-and-data//social-transfers,7531.html, combined with information on programmes in Jamaica and the Bahamas. Stampini and Tornarolli (Citation2012) describe the expansion of CCT programmes in the region; Robles, Rubio, and Stampini (Citation2017) characterise coverage of the poor; and Ibarrarán et al. (Citation2017) describe CCT programme functioning.
2. Originally called Red Solidaria, a new government renamed the programme to Comunidades Solidarias Rurales in 2009. The CCT programme itself did not change substantively.
3. Molina Millán et al. (Citation2019) review the methodological challenges and evidence for the longer-term impacts of CCTs.
4. There is a related debate on the longer-term effects of unconditional cash transfers (Bandiera et al. Citation2017; Banerjee et al. Citation2016; Handa et al. Citation2018; Haushofer and Shapiro Citation2018).
5. Therefore, it also is not feasible to carry out cost-benefit analyses since we only examine a subset of the various possible beneficial outcomes resulting from the CCT.
6. The education transfer eligibility age cut-off was raised to 18 for municipalities entering the programme starting in 2008, but the change is not relevant for our analyses (de Brauw and Peterman Citation2011).
7. To our knowledge, Familias en Acción in Colombia was the only other CCT programme at the time with similarly explicit conditionality on preschool enrolment, but evaluation reports do not directly examine it as an outcome.
8. The transfer amounts were calculated to cover approximately one-quarter of the 2004 monthly minimum wage for agricultural activities, set at $74.10. A single transfer was equivalent to 37 percent of the 2005 Salvadoran monthly per capita rural poverty line (Britto Citation2007). Transfers were combined for delivery every other month.
9. Beginning with urban areas in the high extreme poverty group municipalities, a proxy means test (PMT) based on initial ownership of assets and housing characteristics was used along with the demographic criteria to determine programme eligibility (IFPRI and FUSADES Citation2010). We do not observe the initial information required to estimate the PMT score for families when the programme began. Therefore, we examine only rural areas in this study, where there was no PMT-related eligibility requirement.
10. Closed enrolment was widely enforced. Local programme promoters, however, could request that a nuclear family erroneously excluded during programme incorporation be included. The evaluations provide evidence of a significant negative consequence of closed enrolment, increasing under-coverage of the poor over time (IFPRI and FUSADES Citation2010).
11. By 2014, fewer than two-thirds of original beneficiaries continued to receive transfers (Beneke de Sanfeliú, Angel, and Shi Citation2015).
12. The International Food Policy Research Institute (IFPRI) and the Fundación Salvadoreña para el Desarrollo Económico y Social (FUSADES) carried out the short-term evaluation (IFPRI and FUSADES Citation2008; Citation2009; Citation2010). The identification strategy for the evaluation is not feasible for assessing the accumulated impacts of the programme after several years of operation for two reasons. First, there were no further follow-up evaluation surveys representative of the region after 2010. Second, the 100 poorest municipalities had been included in the programme by 2010, leaving no potential comparison municipalities in the severe or high extreme poverty groups.
13. Dimensions of quality of early schooling appear to have improved over time in early programme years, including school organisation and functioning and teacher attendance (IFPRI and FUSADES Citation2010).
14. Multiple nuclear families in a household make up less than five percent of the sample. Excluding them from the analysis sample leads to negligible changes in estimated results.
15. By the time of the 2012/13 census, of course, the composition of nearly all families would have changed relative to when the programme had begun. For example, some children may have migrated or died, so we cannot determine with certainty the firstborn child for each mother with the available data. For those children who could not be linked to their mother using maternal relationships (because the mother was not co-resident in the same household or was deceased), it is possible to use i) paternal relationships and ii) relationship with the household head or the grandparents to determine if they might be firstborn children. Children assigned to a nuclear family through the maternal relationship comprise 88 percent of the likely firstborn five- and six-year-olds and this is the sample we use. (Paternal relationships yield an additional 2 percent and household head or grandparent the remaining 10 percent.) There is no significant relationship between eligibility status and whether the firstborn child is determined through their mother. The coefficient estimate on the eligibility indicator is −0.026 for the 24-month window for six-year-olds, and 0.010 or smaller for all other samples. Including the likely firstborns determined through paternal and other relationships in the sample leads to similar findings (not shown).
16. To determine the start or incorporation date in each municipality, we use the start of the programme incorporation registry implemented in the municipality. On average, the registry fieldwork within each municipality lasted 45 days. Results reported below change little when we instead set the cut-off based on the last day of interviews in the municipality. The programme incorporation registry is not used more directly in the analyses, however because it does not contain information on children not yet born (our comparison group) nor is it possible to link individuals from it to the 2012/13 programme census.
17. Given limits of statistical power, particularly for the narrower windows, we do not report an examination of possible treatment effect heterogeneity.
18. Even if these cases were known, however, because those who gained access despite being initially ineligible would be a selected group, we would not treat them any differently for the ITT analysis.
19. Summary statistics are similar for samples within the 8- and 12-month windows ( and ) and do not differ between boys and girls (not shown).
20. Children enrolled in school also could benefit from schooling related programmes operating during the period, including a student packet targeted to students in all rural public schools (two uniforms, a pair of shoes and school supplies) and school meals and milk programmes which combined were approximately 0.4 percent of GNP from 2010 onward (Mesa-Lago and De Franco Citation2010; Beneke de Sanfeliú, Lustig, and Oliva Citation2015). In line with higher enrolments due to the programme, these are somewhat higher for eligible children.
21. Because not all children would have had access to preschool, overall average estimated effects reflect effects in communities with and without preschools, which could differ from local average effects in areas with or without preschool.
22. Because we estimate multiple outcomes on schooling for each age group, we also recalculated statistical significance within each age group and window using Bonferroni family wise error rates and the Benjamini and Hochberg (Citation1995) false discovery rates. All effects significant at five percent or lower for five-year-olds remain significant at least at 10 percent.
23. At the same time, this change would come with potentially higher private costs to the family, though on the margin they would likely be small since the main components of private costs to the adults, collecting transfers and time spent in the training workshops, would be unchanged (IFPRI and FUSADES Citation2008).
24. Firstborn placebo tests as in ) are not estimated for wealth in . They are not plausible placebos for effects on the household wealth index, since longer exposure to transfers may enable asset accumulation for the families of six-year-olds, all of whom would have been eligible.
25. Kirk (Citation2016) further examined adult time use patterns by gender in the short term. She found evidence of an increase of about an hour a day in adult male time spent in formal and informal productive work that was largely offset but a reduction for adult females. This is consistent with programme demands on the time of the mother being accommodated by a reduction in other activities.
26. A different concern, that we are unable to investigate empirically due to the lack of exogenous variation in the density of exposure, is the possibility of spillovers on the ineligible population. In theory such spillovers could be positive or negative. However, evidence of related CCT programmes (whose design allows identification of spillover effects through a partial population experiment) generally point to positive spillover effects on educational outcomes (Angelucci et al. Citation2010; Bobonis and Finan Citation2009; Macours and Vakis Citation2018), which would suggest our results provide a lower bound of the actual effects.
27. For migration internal to the municipality, which we also do not observe, the implication for the analysis is that canton-level fixed-effects do not accurately reflect the ITT residential location at the start of the programme. We therefore re-estimate results controlling for the more aggregate municipality-level fixed effects. Results are substantively unchanged ( and ).
28. In the online appendix, we also summarise findings using the 2007 Salvadoran national census to estimate potential short-term effects of the programme on migration rates in the first 32 municipalities receiving the programme in 2005 and 2006, and find they are modest.
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Notes on contributors
John A. Maluccio
Sanchez Chico is at the Organisation for European Cooperation and Development ([email protected]), Macours at the Paris School of Economics and INRAE ([email protected]), Maluccio at Middlebury College ([email protected]), and Stampini in the Social Protection and Health Division at the Inter-American Development Bank (IDB) ([email protected]). Support was provided by the IDB Economic and Sector Work ‘CCT Operational Cycles and Long-Term Impacts’ (RG-K1422). We thank the Government of El Salvador for providing the data and programme materials used for the analysis and María Deni Sanchez for her support throughout. We also thank Teresa Molina Millán, Tania Barham, Pablo Ibarrarán, Norbert Schady, Luis Tejerina, Diether Beuermann Mendoza, Ana Sofia Martinez, participants in presentations at the IDB and anonymous referees for valuable comments. All remaining errors are our own. This paper modifies and extends IDB working paper 908. The content and findings reflect the opinions of the authors and not those of the OECD or of the IDB, its Board of Directors or the countries they represent.