IFPRI Discussion Paper 02262 

July 2024 

The Effectiveness of Cash and Cash Plus 
Interventions on Livelihoods Outcomes 

Evidence from a Systematic Review and Meta-analysis 

Jessica Leight 

Kalle Hirvonen 

Sarim Zafar 

Poverty, Gender, and Inclusion Unit 



 

INTERNATIONAL FOOD POLICY RESEARCH INSTITUTE 
The International Food Policy Research Institute (IFPRI), a CGIAR Research Center established in 1975, 
provides research-based policy solutions to sustainably reduce poverty and end hunger and malnutrition. 
IFPRI’s strategic research aims to foster a climate-resilient and sustainable food supply; promote healthy 
diets and nutrition for all; build inclusive and efficient markets, trade systems, and food industries; 
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integrated in all the Institute’s work. Partnerships, communications, capacity strengthening, and data and 
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The Institute’s regional and country programs play a critical role in responding to demand for food policy 
research and in delivering holistic support for country-led development. IFPRI collaborates with partners 
around the world.  
 

AUTHORS 
Jessica Leight (j.leight@cgiar.org) is a Senior Research Fellow in the Poverty, Gender, and Inclusion 
(PGI) Unit of the International Food Policy Research Institute (IFPRI), Washington, DC. 
 
Kalle Hirvonen (k.hirvonen@cgiar.org) is a Senior Research Fellow in IFPRI’s PGI Unit, Helsinki, 
Finland. 
 
Sarim Zafar (s.zafar@cgiar.org) is a Research Analyst in IFPRI’s PGI Unit, Washington, DC. 
 
 
 
 
 
 
 
 
 
 
 
 
 
Notices  
 
1 Author order is alphabetical. The experiment on which this paper is based is registered in the American Economic Association's 
registry for randomized controlled trials as AEARCTR-0006361. This project received clearance from Makerere University's School 
of Social Sciences Research Ethics Committee (08.20.436/PR1) as well as from the International Food Policy Research Institute's 
Institutional Review Board (DSGD-20-0829). The research was also registered at the Ugandan National Commission for Science 
and Technology (SS603ES). 
 
2 IFPRI Discussion Papers contain preliminary material and research results and are circulated in order to stimulate discussion and 
critical comment. They have not been subject to a formal external review via IFPRI’s Publications Review Committee. Any opinions 
stated herein are those of the author(s) and are not necessarily representative of or endorsed by IFPRI.  
 
3 The boundaries and names shown and the designations used on the map(s) herein do not imply official endorsement or 
acceptance by the International Food Policy Research Institute (IFPRI) or its partners and contributors. 
 
4 Copyright remains with the authors. The authors are free to proceed, without further IFPRI permission, to publish this paper, or any 
revised version of it, in outlets such as journals, books, and other publications.

mailto:j.leight@cgiar.org
mailto:k.hirvonen@cgiar.org
mailto:s.zafar@cgiar.org


iii 
 

Abstract 
 

Over the last 20 years, a burgeoning scholarly literature has analyzed the effects of cash transfer 

and cash plus interventions in a wide range of contexts and using a range of empirical designs. 

We conduct a systematic review and meta-analysis to estimate the pooled effect of any cash or 

cash plus intervention on livelihoods-related outcomes (consumption, income and labor supply), 

ultimately compiling 305 different treatment estimates from 155 treatment arms in 104 studies 

(and in 43 countries). Using random effects and multilevel models, our findings suggest that cash 

transfer programming is associated with an increase of between $1 and $2 in monthly household 

consumption and income per $100 in cumulative transfers, an effect that persists for a period of 

roughly three years (inclusive of the period of program implementation); this effect is 

meaningfully larger (as much as $4 larger) for cash transfer programs that also include a cash-

plus livelihoods intervention. There are no significant effects observed on labor force 

participation. We also present a range of estimates capturing the longer-term (cumulative) effects 

of cash transfers on consumption under alternate assumptions.  



iv 
 

Acknowledgements 
 

This work was supported by the Norwegian Government and the Norwegian Agency for 

Development Cooperation (NORAD) under the project titled, “Learning Support for a Sub-

Saharan Africa Multi-Country Climate Resilience Program for Food Security”, and by the 

donors who fund the CGIAR Research Initiative on Fragility, Conflict and Migration (FCM) as 

well as the CGIAR Initiative on National Policies and Strategies, through their contributions to 

the CGIAR Trust Fund: https://www.cgiar.org/funders/. We thank several IFPRI colleagues for 

useful comments. All errors, views and opinions are our own. 

https://www.cgiar.org/funders/


1 Introduction

In recent decades, cash transfer programs such as conditional cash transfers (CCTs) and

unconditional cash transfers (UCTs) have become increasingly popular, particularly in low-

and middle-income countries (Fiszbein, Kanbur and Yemtsov, 2014; Gentilini, 2022). The

primary goal of these programs, as stated by national governments, international develop-

ment agencies, and humanitarian organizations, is to assist poor households in meeting basic

needs and escaping extreme poverty (Fiszbein and Schady, 2009; USAID, 2022; WFP, 2023).

Cash transfers allow flexibility by permitting recipients to finance immediate consumption

needs or to increase future income streams through investments and savings. They are also,

in general, an intervention that is feasible to implement and scale across a range of contexts

(Gentilini, 2016, 2022).

A wide range of available evidence — explored extensively in this systematic review and

meta-analysis — shows that cash transfers are highly effective in reducing poverty in the

short run, but the limited literature analyzing medium or long-run effects of cash transfers

suggests more mixed evidence around the sustainability of these effects following the cessation

of cash payments (Blattman, Fiala and Martinez, 2020; Haushofer and Shapiro, 2018). “Cash

plus” interventions then couple transfers with complementary interventions aiming to help

households enhance their existing livelihood activities or to diversify into new activities

to break the cycle of chronic poverty and build resilience; the use of cash plus is often

motivated in part by the goal of making the effects of cash more sustainable (FAO, 2018).

Examples of common cash plus interventions include training on financial literacy or business

management, or provision of assets like livestock and/or large lump sum cash to launch

income generating activities. Importantly, these marginal benefits will most plausibly be

observed in a context where viable income-generating activities exist, and may be accordingly

attenuated in fragile or conflict-affected contexts where local economic activity is disrupted

and complementary public services are largely absent (Lind, Sabates-Wheeler and Szyp,

2023).

Over the last 20 years, a growing body of research has evaluated the impact of both

cash and cash-plus interventions in a wide range of settings, using both experimental and

non-experimental methods. Our goal here is to systematically review and meta-analyze the

literature analyzing the effects of all forms of cash and cash plus interventions on livelihoods-

related outcomes (defined to be consumption, income, and labor force participation). The eli-

gibility criteria for inclusion in the review thus require an experimental or quasi-experimental

causal analysis of a cash or cash plus intervention (compared to a control or status quo with-

1



out cash) conducted in a low-or middle-income country analyzing one of the outcomes of

interest. We also seek to examine how these effects vary in different contexts and when

analyzed using different experimental designs; and assess any potential bias in this literature

introduced by selective reporting (the “file–drawer problem”).

Following a comprehensive and structured search of both published and unpublished

literature, our review includes 104 studies encompassing 155 different treatment arms, of

which 26 arms coupled cash with livelihood related activities. Using this sample, we then

characterize all cash transfer programs in terms of the cumulative transfer received by sample

households, and meta-analyze all treatment effects as the linear effect of $100 of cumulative

cash (with or without supplemental cash plus interventions) on the specified outcome of

interest using standard random effects and multilevel meta-analysis models. Consumption

and income are specified as monthly household aggregates, and all monetary estimates are

converted to 2010 U.S. dollars in purchasing power parity terms.1

The sample of studies and programs represented encompasses a huge range of cash trans-

fer programs implemented around the world (Mexico is the most commonly represented

country, but sub-Saharan Africa the most commonly represented region) and by a range of

actors. It includes long-running and widely known government transfer programs such as

PROGRESA and much smaller, targeted programs implemented by non-governmental orga-

nizations. More specifically, the sample of programs analyzed is characterized by a median

cumulative transfer of $850 in 2010 PPP; for a plurality of transfers (64%), this cumula-

tive amount was disbursed monthly or bi-monthly, with lump-sum transfer structures also

common (21%). The median duration of the intervention in our sample (inclusive of cash

disbursements and any cash plus programming) is 19 months, though there is wide hetero-

geneity. In terms of the duration of follow-up, 53% of the evaluations are reporting on cash

transfer programs that are ongoing at endline, and within the subsample of those report-

ing on cash transfers that are not ongoing, the median period observed following the final

transfer is 13 months, suggesting the majority of these estimates are capturing short-term

effects.2

Our primary findings suggest that cash transfers lead to an increase of around $1.50 to $2
in monthly household consumption and income per $100 transferred, at a median follow-up

1Much of our analytical strategy here follows Kondylis and Loeser (2021) and Crosta et al. (2024), and
we describe how our meta-analysis builds on these papers and contributes to the broader literature in further
detail below.

2For papers that reported multiple rounds of data, we extracted effect estimates from the final round,
implying we already are capturing the upper bound of the follow-up period.

2



point of 24 months following the first transfer (or five months following the last transfer,

with evaluations implemented for ongoing programs coded as zero months following the last

transfer). We find no economically meaningful effect (positive or negative) of cash transfers

on labor force participation for a pooled sample or samples of men and women. Moreover,

we find no meaningful difference in the results between programs that were ongoing at

the point of follow-up measurement and those that had already concluded. This suggests

no pronounced decay in cash effects within the relatively short follow-up periods generally

observed in this set of estimated effects. 3

When we examine variation across transfer types, we find that cash plus livelihoods

interventions are, on average, more effective, yielding an additional marginal effect of $4 -

$5 per $100 transferred relative to the estimated cash-only effect. We find no significant

difference in the effects between unconditional and conditional cash transfers. Lump sum

transfers generally have a smaller effect on consumption, as do programs implemented by

governments, though these patterns are not fully consistent. We also analyze variation

in effects by context. In general, the effects of cash transfers are somewhat smaller in

sub-Saharan Africa, the most common site of studies included in this review. There is no

evidence of any differential effects in contexts that are fragile and/or conflict-affected (using

the World Bank definition); however, the body of evidence is extremely limited, as only 14

studies including 42 intervention arms (and only four cash plus arms) were evaluated in a

fragile setting. This highlights a clear evidence gap.

For evaluation methods, we cannot reject the null that randomized controlled trials

(RCTs) yield the same effect sizes as other evaluation methods. However, studies that

use regression discontinuity (RD) designs consistently report smaller effect sizes, presum-

ably reflecting the fact that RD methods quantify a local average treatment effect around

the program eligibility threshold that may not be applicable to all eligible households, many

of which are considerably poorer.

To contextualize our estimates in terms of the magnitude of the estimated effects on

consumption, we note that the structure of our analysis estimates the effect of a cumula-

tive stock of cash transfers (total amount transferred) on a flow measure of consumption

(per household per month); accordingly, the key question is how long these consumption

effects persist. While the structure of this analysis does not allow us to directly estimate

this time horizon, we can draw on general stylized facts: the average program duration is 19

3We cannot provide any systematic evidence around the longer-term persistence of cash effects, though
we discuss the implications of some different assumptions around persistence in the Discussion section.

3



months, and the average measured post-program follow-up period (conditional on an evalu-

ation following program completion) is 13 months, with little evidence that effects fluctuate

or attenuate during this period. Accordingly, we estimate that the program effects persist

for roughly 2.75 years, implying a total consumption effect in the range of $50 per $100
transferred.

We also explore a range of other scenarios with alternate assumptions around the longer-

term persistence of effects, discounting of these longer-term effects, and variation in the main

treatment effect estimates. In general, this analysis suggests cumulative effects between $40
and $70 per $100 transferred for modalities that are cash only (UCTs, CCTs) or primarily

cash (cash plus a non-livelihoods intervention).4 We discuss a range of reasons why the

effect of transfers on consumption appears to be other than one-to-one: implementation er-

rors leading to true transfer receipt being lower than estimated transfer receipt; household

use of transfers for investments with low returns or returns observed only in the medium-

term; and transfers directed to expenditure categories not typically captured in consumption

aggregates. Re-estimating the same analysis for a cumulative effect of $100 cash transfers

delivered as part of cash plus livelihoods programming suggests a meaningfully higher cumu-

lative effect — from a range of $80 to $100 up to $500 — but these more optimistic impact

estimates must also be weighed against considerably higher costs for cash plus programming.

While these costs are often not reported, the limited estimates available suggest that the

costs of some more intensive cash plus programming may be comparable to, or higher than,

the estimated cumulative benefits.

Finally, we use methods from both health and economics (Egger et al., 1997; Brodeur,

Cook and Heyes, 2020) to assess non-reporting (publication) bias in the sample of studies

analyzed. We find substantial evidence of publication bias of equal magnitude in both

the RCT and non-RCT literature, suggesting that there may be some meaningful risk of

overestimating the effects of cash on consumption and income if noisily estimated null and

negative effects are missing from the sample.

Our research builds on and contributes to a previous meta-analytic literature aggregating

the impact of cash transfers on livelihood outcomes (as summarized in Table A1).5 Our

4These aggregated estimates are somewhat lower than those reported in the context of PROGRESA in
Mexico. Gertler, Martinez and Rubio-Codina (2012) estimate that the average PROGRESA beneficiary
household consumes 74 percent of the transfer and invests the remainder.

5Another growing body of research evaluates the impact of cash transfers on non-economic outcomes.
Meta-analyses of these effects have aggregated the impact of cash transfers on health outcomes, such as
children’s nutritional outcomes (Manley et al., 2020; Manley, Alderman and Gentilini, 2022; Little et al.,
2021), mental health (McGuire, Kaiser and Bach-Mortensen, 2022; Wollburg et al., 2023), and neglected

4



study is closest to Kondylis and Loeser, 2021 who conduct a meta-analysis of randomized

controlled trials of temporary UCTs and contrast their impacts vis-a-vis “Targeting the Ultra

Poor” (TUP) programs, multifaceted graduation programs combining large asset transfers

with intensive livelihood training.6 A second comprehensive recent meta-analysis of RCTs

evaluating UCT programs only is Crosta et al., 2024, a paper that reports on a wide-range

of outcomes, including consumption, income, assets, labor force participation, child health,

schooling and mental health, but does not consider cash plus programs.

By contrast, the scope of our meta-analysis is broader and the focus is somewhat differ-

ent, offering a number of contributions to the existing meta-analytic literature. First, our

definition of cash-plus is not restricted to the most intensive and successful graduation pro-

grams. Second, we consider both UCT and CCT programs and do not limit the evaluation

methodology to RCTs only. In our sample, over half of the UCT interventions occurred in

sub-Saharan Africa, whereas only 16 percent of the CCT programs were implemented there.

Consequently, a focus on UCTs implies a sample concentrated in sub-Saharan Africa, without

drawing on evidence from many long-running large-scale CCT programs in Latin America

(Fiszbein and Schady, 2009). Moreover, the focus on RCTs implies a sample that overrepre-

sents NGO-implemented programs, as many government programs are not randomized and

thus the evaluations necessarily employ other designs.

In particular, the decision to limit the sample to RCTs presents an important trade-off.

Evaluations of government-implemented programs generally report smaller effects compared

to those of NGO-implemented programs (Vivalt, 2020) – possibly because they typically

operate at scale, making them more challenging to implement effectively (Muralidharan and

Niehaus, 2017). However, our risk-of-bias assessment reveals that, as expected, non-RCTs

typically have a higher risk of bias, on average, than RCTs. To address this trade-off, we will

explore sensitivity of our main findings to the inclusion or exclusion of non-RCT designs.

Finally, we assess the degree of publication bias in this literature, which constitutes another

unique contribution relative to the earlier meta-analyses in this space.

tropical diseases (Ahmed et al., 2022). Similarly, other studies have conducted meta-analyses of the impact
of cash transfers on educational attainment (Baird et al., 2013; Garćıa and Saavedra, 2017), temptation
goods, such as alcohol or tobacco (Evans and Popova, 2017), and intimate partner violence (Baranov et al.,
2021).

6Correa et al., 2023 also contrast cash only interventions against cash plus interventions in their meta-
analysis, but focus on programs implemented in rural Africa and consider a different set of outcomes such as
asset accumulation and labor allocation. Their meta-analysis is also considerably smaller in terms of scope,
covering 16 cash only interventions and 12 cash plus (including graduation programs) interventions.

5



2 Methods

2.1 Search strategy and selection criteria

The inclusion criteria for this review included the following: we aimed to aggregate experi-

mental or quasi-experimental quantitative analyses probing the effects of cash or cash plus

programming on livelihoods outcomes in low- and middle-income countries relative to a com-

parison group that does not receive cash.7 An experimental or quasi-experimental design is

one including a plausible counterfactual design: in practice, this encompasses randomized

controlled trials, regression discontinuity analyses, and difference-in-differences and matching

designs. Following our initial overview of the literature, we defined livelihoods outcomes to

include consumption (total consumption, food consumption, or non-food consumption); in-

come; and labor force participation. Consumption and income will ultimately be defined and

analyzed at the household level; labor force participation is defined at the individual level,

and will be analyzed for pooled samples of adults as well as for men and women separately.

Interventions are eligible only if they include at least some disbursement of cash (in any

installment or form). Thus interventions that provide only asset, food, or other in-kind

transfers are not eligible. Public works interventions programs in which cash is provided

in exchange for work (e.g., MGNREGA in India or the Productive Safety Net Program in

Ethiopia, or other similar interventions) are likewise ineligible. Any multifaceted interven-

tion including additional programming that supplements cash (including but not limited to

training, behavioral change communication, and asset or food transfers) is eligible. Some

trials may include multiple arms in which some meet the eligibility criteria for this review

and some do not (e.g., a comparison of cash and food transfers vis-a-vis a control arm); in

that case, we retain and analyze data only from the eligible arms.8

With respect to the experimental design, the review criteria entails the exclusion of

papers that are purely qualitative; papers that report on small-scale pilots (e.g., with fewer

than 200 observations); analyses that do not compare outcomes using a plausible control

or comparison group; and papers that do not include a control or comparison group with

minimal programming (and no access to cash). Thus trials that include multiple arms in

7We follow the World Bank classification of countries as low- or middle-income, and use the classification
from the year in which a particular study was launched. Thus studies from Chile and Uruguay, both now
categorized as high-income countries, remain eligible since they were conducted prior to the year (2013) in
which both countries were re-designated as high-income.

8The reason for this exclusion is that we do not have a systematic sample of papers analyzing, for
example, food transfers, and thus any aggregation of evidence from the limited selection of arms analyzing
food transfers observed in trials that also analyze cash transfers will inevitably be of limited value.

6



which all arms receive cash, with some variation in modality or supplemental programming,

are ineligible. Trials in which there is a delayed phase-in of cash and the control arm

corresponds to recipients who will receive cash following the endline assessment are eligible.

In addition, the criteria exclude papers that do not report at least one of the outcomes of

interest for a general sample; thus papers that report the effects of cash transfers only on

educational, nutritional, or human capital outcomes, or on livelihoods outcomes other than

those identified here, are excluded.9

We identified papers eligible for the review by conducting a structured search in multiple

databases: Web of Science, ScienceDirect, EconLit, and the 3ie database of evaluations, and

Google scholar. Our search strategy entailed various combinations of terms capturing the

interventions of interest (cash transfer, cash grant, UCT, etc.); the experimental designs of

interest (RCT, regression discontinuity, etc.); and, when feasible, the outcomes and contexts

of interest. The detailed search strategy is provided in Table A2 in the Appendix. The

references generated by all database searches (10,726 total records) were compiled in Rayyan,

where duplicate-detection, keyword-based screening and title and abstract screening were

conducted by SZ (see appendix for details). We then added papers from our Google Scholar

search and also added some papers manually by cross-checking the papers cited in three other

recent systematic reviews (Correa et al., 2023; Crosta et al., 2024; Kondylis and Loeser,

2021).10 Full-text screening was conducted by KH and SZ, with JL double-screening a

random subsample. Any discrepancies were resolved by discussion.

2.2 Data extraction and cleaning

We conducted the meta-analysis based on study reports and did not draw on individual

participant data. We extracted data using a customized form, including the study design;

descriptive data on the intervention, including the types of any cash plus programming

implemented; the timeline (duration of the intervention’s implementation and its timing

vis-a-vis any survey assessments): the setting (country, region, urban/rural, and whether

the context is fragile or conflict-affected); the sample and type of data collection; and the

estimated effects for all relevant outcomes reported, as well as standard errors or confidence

intervals.

Given our interest in identifying fragile and conflict-affected settings in this analysis, we

9By general sample, we refer to a broad sample of eligible households or adults; there is also a substantial
literature that analyzes the effects of cash transfers on the labor supply of children or adolescents, and those
papers are likewise excluded here.

10We reviewed the first approximately 150 records identified in Google Scholar to assess their inclusion.

7



draw on the World Bank classification at the country level, reported by year back to the

year 2006. We code a particular study as fragile or conflict-affected if the country site was

identified as such in the baseline year of the study.11 We also supplement this by manually

identifying studies that are conducted with refugee samples, given the inherent fragility

experienced by these samples; or that motivate their study around themes of conflict, as

identified by the use of the word conflict in the title or abstract.

We assessed studies’ risk of bias at the study level; for randomized controlled trials, we

used the Cochrane risk-of-bias tool (Higgins et al., 2019), and for quasi-experimental studies,

we used the JBI 12 risk-of-bias tool (Barker et al., 2024). For RCTs, the five domains assessed

are the randomization process, deviations from intended interventions, missing outcome data,

measurement of the outcome, and selection of the reported result. For non-RCTs, the eight

domains assessed are clarity about cause and effect, similar pre-intervention, environment

similar over time, sufficient pre- and post- measurements, complete follow-up, consistent

measurement, appropriately powered, and tests of no violations of assumptions. Using in-

formation about risk of bias, we also generate a variable corresponding to high risk of bias

if at least three domains are characterized by some or high risk of bias (out of five domains,

for an experimental study, or out of eight domains, for a non-experimental study). Note

the higher (proportional) threshold for risk of bias for experimental studies is also defined in

light of the fact that it is extremely common for experimental studies to be characterized by

high risk of bias in the fifth domain, corresponding to selective reporting, given that a large

number of these studies were launched prior to the widespread adoption of preregistration

or pre-analysis plans for trials in economics.13

If results were reported for multiple follow-up periods, the estimated treatment effects

for the longest follow-up period were extracted. If results for multiple specifications were

reported, we extracted the specification that was identified by the authors as of primary

interest or the most robust specification; or, if this was not clearly designated in the text,

we used our own judgment to identify a preferred or more robust specification. If results for

specifications with and without additional covariate controls were reported, we preferentially

11A number of studies in the sample had a baseline year prior to 2006; these studies are all in contexts
that were never, at any point, identified as fragile or conflict-affected (e.g., Mexico). Accordingly, we feel we
can confidently code these settings as non-fragile.

12Formerly known as the Joanna Briggs Institute, JBI is an international research organisation based at
the University of Adelaide in Australia.

13For some quasi-experimental designs, particularly regression discontinuity, three domains pertaining to
variation and trends over time are not applicable, and thus the relevant criteria is at least three domains out
of six are characterized by some or high risk of bias.

8



extract the results estimated without additional controls; however, in practice the majority of

effect estimates correspond to effects estimated conditional on same baseline controls. When

relevant data were not available in published study reports, JL contacted study authors up

to two times to request missing information.

We also focus on extracting intent-to-treat effects. While some recent meta-analyses of

cash transfers (Kondylis and Loeser, 2021) and educational interventions (Angrist and Mea-

ger, 2023) have emphasized the value of meta-analyzing treatment on the treated effects, cash

transfers (and closely related interventions such as cash for public works employment) are an

intervention for which there is robust evidence of local spillovers, in some cases positive (Eg-

ger et al., 2022; Angelucci, Attanasio and Di Maro, 2012; Franklin et al., 2021; Muralidharan,

Niehaus and Sukhtankar, 2023) and in some cases negative (Beegle, Galasso and Goldberg,

2017; Haushofer and Shapiro, 2016; Filmer et al., 2021). Accordingly, estimating a treatment

on the treated effect for cash transfers is not possible without substantial additional assump-

tions around the structure of spillover effects; and meta-analyzing treatment-on-the-treated

effects is infeasible.

Our primary effect measure for this analysis is the estimated coefficient β from a linear

regression capturing the effects of cash on outcomes of interest. First, we normalized all

coefficients for continuous variables (consumption and income) to correspond to a linear

estimate of the effect of a transfer on a monthly variable at the household level. Estimates

reported as normalized coefficients (in standard deviations) or in logs were converted to linear

coefficients using data provided about the mean and standard deviation of the outcome of

interest in the control arm. Second, we converted estimates reported per capita or per

adult equivalent to estimates at the household level using the reported household size, and

estimates reported for other time periods (daily, weekly or yearly consumption or income)

were converted to monthly. Third, all coefficient estimates were converted to 2010 purchasing

power parity-adjusted U.S. dollars. For some papers, additional assumptions were required to

execute these calculations; and in some cases, essential information was simply not available

and thus the paper could not be included in the meta-analysis (though it is still documented

in the systematic review). More information about data cleaning and harmonization is

provided in Section A2 in the Appendix.

For the binary variables corresponding to labor force participation, the only required

cleaning was to convert standardized effect estimates or effect estimates generated using

probit or other non-linear models into coefficients corresponding to linear models.

A parallel process was implemented to generate estimates of transfer size, with the ob-

9



jective of estimating the full value of the transfer received by households in the analytical

sample during the analytical period of interest (generally, between two rounds of assess-

ment).14 In cases where transfers varied in amount based on different household criteria

— typically, demographic criteria such as the number of children or other socioeconomic

characteristics — we preferentially used estimates provided in the paper text of the average

transfer received by sample households. If no such estimate was available, we attempted to

construct one using other available data (i.e., average household size or typical number of

children); and for conditional cash transfers, these estimates were constructed assuming that

the payment conditions were satisfied. The estimates of transfer size were again converted

to 2010 U.S. dollar purchasing power parity estimates.

The final step entailed the construction of normalized coefficients capturing the effect per

dollar of transfer. For the purposes of exposition, we will present these effects multiplied

by 100, or the effect of a (cumulative) $100 transfer. We calculate cumulative transfer

values given the wide and complex variation in transfer structure, and will analyze effects

on monthly household consumption and income given that these are standard economic

measures of interest in the literature; this does imply that we are effectively analyzing the

effect of an accumulated stock of cash transfers on a flow measure of monthly household

consumption. This is consistent with other recent work in the cash meta-analysis literature

(Crosta et al., 2024; Kondylis and Loeser, 2021), but we also discuss in some detail in

Section 4.1 below how to re-interpret our findings as a causal effect on a cumulative measure

of consumption.

2.3 Meta-analysis estimation

First, we estimate a random-effects meta-analysis model using the restricted maximum like-

lihood method; we estimate this model separately for each outcome of interest, employing all

available coefficients (from all relevant arms) from each trial, and present the results in forest

plots.15 We assess between-study heterogeneity using the I2 statistics. Given that there are

some effect estimates that are extremely large, we also present meta-analysis estimates that

exclude outliers, defined as effect estimates above the 97th percentile.

14Thus for transfer programs that may have been ongoing, the aim was to estimate how much the average
household would have received by endline, since baseline or since the inception of their eligibility. However,
information about the timeline of cash receipt and whether or not a transfer program was ongoing was often
imprecisely specified.

15The assumptions for a fixed-level meta-analysis (that all studies shared a common effect size, and factors
influencing this size are consistent across studies) does not plausibly hold in this context.

10



Second, we estimate a multi-level (three-level) random-effects model that accounts for

the dependence across multiple treatment effects estimated for the same program (Moeyaert

et al., 2017; Van den Noortgate et al., 2015). We also estimate this model using two different

strategies. In our first and preferred strategy, we seek to link treatment effect estimates

generated by evaluation of the same program in the same country. Accordingly, if a paper

reports estimates of multiple different programs in different countries in a single analysis,

we now code the analysis implemented in each country as a separate trial; and conversely,

we code all estimates of the impacts of (for example) PROGRESA as part of an evaluation

of a single program, to capture the presumed dependence across effects. In the second

analysis conducted as a robustness check, we simply use published papers to define trials:

thus a published paper including multiple estimates from different countries is coded as one

trial, and conversely, two separate papers reporting analyses of the same intervention (i.e.,

Progresa or another frequently-analyzed cash transfer program) are coded as two separate

trials.16

We then present meta-regressions that analyze how characteristics of the context, trans-

fer, and study moderate the observed effect sizes. We will estimate meta-regressions only

for the outcomes of total consumption and food consumption, as these are the outcomes for

which the sample size is largest. The characteristics of interest include two binary variables

capturing the context (a binary variable equal to one for sub-Saharan Africa, and a binary

variable equal to one for a fragile or conflict-affected context); four variables capturing char-

acteristics of the transfer (a binary variable equal to one if the transfer is implemented by

government, a binary variable equal to one for a conditional cash transfer, a binary variable

equal to one for a lump-sum or near-lump-sum transfer, and a binary variable equal to one

for a cash plus livelihoods program); and two variables capturing the study design (a binary

variable equal to one for a regression discontinuity design, and a binary variable equal to

one for a randomized controlled trial).17 We again estimate meta-regressions using both the

16To cite concrete examples, Banerjee et al. (2015) reports the results of a graduation model intervention
evaluated in six countries; in our first analysis, this is treated as a series of separate trials, and in the second
analysis, these estimates are linked as part of the study. Conversely, there are three papers in our sample that
report effect estimates of the Child Support Grant in South Africa (Mostert and Vall Castello, 2020; Scarlato
and d’Agostino, 2019; d’Agostino, Scarlato and Napolitano, 2018); in our first analysis, these estimates are
treated as part of the same trial, and in the second, they are treated as independent estimates.

17A lump sum transfer is defined as a transfer with three or fewer installments in a short period of time,
roughly six to nine months. This is broadly similar to the definition employed by Crosta et al. (2024), who
define a lump sum transfer as no more than three installments within no more than two months; however, we
slightly lengthen the timeline to encompass the structure of GiveDirectly transfer programs. These transfers
are generally defined as lump-sum, but are also inclusive of a first “token” transfer that is separated from
the final transfer by up to eight months (Egger et al., 2022); there are also some lump sum cash transfer

11



simple random effects and multilevel model.

3 Results

3.1 Sample and descriptive statistics

The screening process included an initial review of 10,726 records; Figure 1 summarizes

the screening steps. Full-text screening was conducted on 381 separate records, and this

ultimately yielded a sample of 104 studies for inclusion in the meta-analysis, including 155

different treatment arms and 310 treatment effects for the variables of interest. The largest

samples for specific indicators are for total consumption and food consumption, reported in

68 and 67 treatment arms, respectively. Details are summarized in Table 1. There are seven

studies for which insufficient information about the econometric analysis or the transfer was

provided in the paper (and no supplementary information was provided by the authors), and

these studies are excluded from the meta-analysis; more information is provided in Table A3

in the Appendix. Table A4 summarizes all of the studies included in the systematic review.

Figure 2 summarizes the geographic distribution of the evidence included in the system-

atic review,18 drawn from 43 unique countries. Mexico is the most commonly represented

site, included in 12 studies, followed by Kenya (eight), Uganda (eight), and Malawi (seven).

Figure 3 summarizes how the geographic composition of evidence has shifted over time, with

each study coded with respect to its baseline year. The earlier body of evidence (stud-

ies characterized by a baseline year prior to 2010) was overwhelmingly dominated by Latin

America, but this has rapidly shifted to a literature increasingly dominated by evidence from

sub-Saharan Africa.

Evidence in fragile or conflict-affected settings, however, is quite limited. There are nine

studies identified as such based on the core World Bank coding, and an additional four

identified using a sample of refugees (two) or a motivation around conflict (three).19 The

programs in our sample where the final transfer was somewhat delayed by the pandemic.
18Note that there are some multicountry studies in the sample, and for those studies, each site is mapped

separately; this leads to a total of 122 country sites represented.
19The nine studies include one conducted in Afghanistan (Kashefi and Naito, 2023), one in Cote d’Ivoire

(Marguerie and Premand, 2023), three in Lebanon surveying Syrian refugees (Salti et al., 2022; Altındağ
and O’Connell, 2023; de Hoop et al., 2018), one in Myanmar (Maffioli et al., 2023), one in Sierra Leone
(Rosas, Acevedo and Zaldivar, 2022), one in Somalia (Ali et al., 2022), and one in Yemen (Kurdi, 2021). The
studies including refugee populations were conducted in Uganda (Gupta et al., 2024) and Colombia (Hidrobo
et al., 2014) and three papers analyze a cash transfer implemented in a conflict-affected region of Uganda
and explicitly motivated with reference to the salience of local conflict (Blattman, Fiala and Martinez, 2014;
Calderone, 2017; Blattman, Fiala and Martinez, 2020).

12



full sample of 14 studies in sites identified as fragile or conflict-affected includes seven in

sub-Saharan Africa, two in Asia, four in the Middle East, and one in Latin America.

Figure 4 then summarizes the 155 separate interventions analyzed, showing how the com-

position of interventions analyzed has shifted over time (again, when each study is indexed

by its baseline year). Our primary classification identifies transfers as a conditional cash

transfer or unconditional cash transfer, implemented either in isolation or in conjunction

with a supplemental intervention that is focused on enhancing livelihoods outcomes or a

supplemental intervention that has a different, non-livelihoods-related objective.20 The full

sample includes 79 UCTs, representing a slight majority of the interventions evaluated; 38

CCTs; 13 UCTs implemented in conjunction with livelihoods-focused interventions; 13 CCTs

with livelihoods-focused interventions, nine UCTs with other interventions; and two CCTs

with other interventions; as well as one intervention not easily categorized.21 The early body

of evidence is dominated by conditional cash transfers (as noted above, largely implemented

in Latin America), with the evidence around unconditional cash transfers growing sharply

after 2005 and becoming the most common form of evidence beginning in 2010.

Figure 5 then summarizes the incidence of various intervention types by region: condi-

tional cash transfers clearly dominate in Latin America, while unconditional cash transfers

dominate in sub-Saharan Africa. Within the sample of studies conducted in fragile and

conflict-affected contexts, there are 14 interventions implemented and they are again dom-

inated by unconditional cash transfers (12). Approximately two-thirds of the interventions

were primarily implemented by governments and one-third by another implementer, typi-

cally an NGO (as summarized in Figure 6). All but one CCT intervention were implemented

by governments, while about half of the UCTs were implemented by governments and the

other half by NGOs. Cash plus programs were more likely to have been implemented by an

NGO.

Figures 7 and 8 summarize the primary characteristics of transfers in terms of their

periodicity and duration. A majority of transfers (63%) are structured to be monthly or

bimonthly (the distinction between these two is not always clearly delineated), though lump-

sum transfers are also common (23%). The median number of payment tranches received by

20A typical example of a livelihoods-focused supplemental intervention would be training or the forma-
tion of savings groups; a typical example of a non-livelihoods focused supplemental intervention would be
information or behavioral change communication related to nutrition or health.

21Azeem, Mugera and Schilizzi (2019) conduct a pooled analysis of the effects of social protection in
Pakistan, including households / individuals participating in a range of different programs with different
characteristics and different criteria. It is not possible to categorize the transfer type here; nor is it possible
to estimate the amount of the typical transfer. Accordingly, this paper is excluded from the meta-analysis.

13



recipients is 10, and the median duration of the intervention (during which these tranches

are disbursed and any supplementary interventions conducted) is 19 months, with wide

heterogeneity (the 25th percentile is six months and the 75th percentile 24 months, with

minimum and maximum of one and 174 months, respectively). The median time elapsed

between the first payment and the period in which outcome data is collected or measured

is 24 months (summarized in Figure A1, implying then a relatively short median gap (five

months) between the final payment and outcome measurement: in other words, this sample

is generally capturing short-term effects, and in fact 53% of the evaluations are reporting on

cash transfer programs that are ongoing at endline.22

Over the intervention period, the median total transfer amount is $850 in 2010 PPP terms

(25th percentile of $424 and 75th percentile of $1495); the distribution is also characterized

by substantial extreme values, and thus we present histograms with and without transfer

amounts above the 95th percentile of the distribution in Figure 9. The median amount

per tranche is around $90 (25th percentile $35 and 75th percentile $258), and again we

present figures with and without extreme total transfer values. Figure A2a and A2b in the

Appendix further summarize the average magnitude of transfers by type. Here, it is evident

that interventions including a cash plus intervention focused on enhancing livelihoods are

generally characterized by total transfer amounts that are meaningfully smaller in comparison

to transfers that do not have this characteristic: the mean transfer amount is less than half

the mean transfer amount for simple cash transfers, and the gap widens further if lump-

sum transfers are excluded. This difference primarily reflects the inclusion in the “cash

only” category of a number of long-term social protection programs such as PROGRESA in

Mexico or the child grant in South Africa, where households can receive ongoing support for

many years and thus the estimated total transfer is substantial.

Moving on to the empirical designs employed in this literature, Figure 10 summarizes the

study types in the sample. Within the 104 studies included, there are 45 cluster-randomized

and 11 individually randomized trials, 16 studies implemented using a regression discontinu-

ity, eight implemented using propensity score matching, and 20 using difference-in-differences

designs. (Four have other designs or report on multiple interventions using different designs.)

Figure 10a summarizes the composition of study designs over time, using data at the level

of the intervention; while cluster-randomized trials were virtually always the most common

22This estimate should, however, be generously caveated: it is surprisingly common for papers to fail to
note explicitly whether the households included in the sample are in fact continuing to receive the transfer
of interest at endline (a point that is related to, but distinct from, the question of whether the program is
ongoing).

14



form of evaluation, their incidence also begins to sharply increase around 2010.23 Figure 10b

summarizes the evaluation design according to implementer type: just over half (51%) of

the government implemented interventions were evaluated using an RCT design, while the

corresponding share for NGO implemented interventions was 76%.

Figure 11 then summarizes our overall assessment of study risk of bias. Within the non-

RCT sample, we assess 27 of 48 studies (a majority) to be characterized by high risk of

bias, a judgment driven by the studies using difference-in-differences and propensity score

matching designs. Within the RCT sample, by contrast, we assess 46 of 66 studies to be

characterized by low risk of bias. Figures A3a and A3b summarize the number of studies

characterized by bias in each domain for both quasi-experimental and experimental studies.

For quasi-experimental studies, the domains characterized by highest risk of bias were tests of

no violations of assumptions (11 studies identified as characterized by high risk of bias) and

similar pre-intervention (six studies). For experimental studies, as previously noted domain

five was characterized by an unusually high number of studies (30) identified as characterized

by high risk of bias in this domain particularly (not across all domains) due to the absence

of a preregistration or pre-analysis plan; many of these studies were launched prior to the

widespread adoption of these tools in economics. Outside of this domain, there was no

other in which there were a significant number of randomized controlled trials identified as

characterized by high risk of bias.

Within the sample of 104 studies, 86 or 83% are published journal articles; the remaining

17% are working papers or technical reports.24

3.2 Meta-analysis findings

The main findings from the meta-analysis are presented in Table 2 and the corresponding

forestplots are presented in Table A4 through A14. In general, we label each study using

the author-date citation and a notation as to the type of intervention (UCT, CCT, UCT+

Livelihoods, CCT+ Livelihoods, UCT+ Other, and CCT+ Other). For papers that include

multiple treatment arms with the same intervention type, we add additional information

to distinguish the arms that pertains either to the location in a multicountry or multisite

23Summarizing this data at the intervention level allows us to capture the cases in which one study includes
multiple study designs, and to also capture the relative volume of evidence — in terms of effect estimates —
generated in studies of different types.

24In some cases, the automated search strategy generated a working paper instead of or in addition to a
peer-reviewed publication reporting the same results; in those cases, we always privilege the peer-reviewed
publication and exclude the working paper.

15



study; the relative size of the transfer (small, medium, large, etc.); or, if there are multiple

arms differentiated only by the specific type of cash plus intervention, for example, they are

labeled with numbers.

For total consumption (Figures A4 and A5), the pooled coefficient estimate suggests that

a $100 transfer leads to an increase of $1.99 in monthly household total consumption, or $1.62
when outliers are excluded. For food consumption (Figures A6 and A7), the comparable es-

timates are $2.13 and $1.76, respectively; and for non-food consumption (Figures A8 and

A9), the pooled effect estimates are $13.55 and $0.61. Note that the samples for all three

indicators are somewhat different, accounting for the larger effect observed on food consump-

tion; and as the sample of effect estimates is considerably smaller for non-food consumption,

a small number of outliers are considerably more influential. For income (Figures A11 and

A11) the impact estimates are $2.13 with outliers and $1.50 without outliers. Overall, this

evidence is fairly consistent and suggests a reasonable inference of an effect of around $1.50
on consumption or income per one hundred dollars of transfer, with the majority of this

effect driven by increased food consumption. We interpret the magnitudes of these effects

in the next section.

For labor force participation (Figures A12 and A13), the pooled coefficient both with

and without outliers suggests a positive, but tiny effect on labor force participation: an $100
transfer is associated with a .00001 increase in the probability of working; despite its tiny

magnitude, this effect is significantly different from zero given the precision generated by a

large number of estimates included. Despite its statistical significance, however, this effect

is clearly far too small to be economically meaningful. This is contrast to both an earlier

hypothesis that cash transfers might serve to reduce labor supply or economic activity, a

hypothesis largely disproven in earlier literature (Handa et al., 2018b; Banerjee et al., 2017),

and to the evidence provided in Crosta et al. (2024) of a positive effect of transfer on labor

supply, a finding that we do not observe in this sample.25 Figure A14 shows the estimated

effects for labor force participation estimated for samples of men and women separately, and

here the effects are weakly negative and statistically insignificant. Note that we cannot rule

out a response on the intensive margin (number of hours or days worked), as we do not

analyze this outcome.

Note that for all meta-analysis estimates, the I2 is high (100%); I2 describes the per-

centage of the variability in effect estimates that is due to heterogeneity rather than random

25We also do not observe this effect in the subset of randomized trials of unconditional cash transfers in
our sample.

16



variation in the sample (Cumpston et al., 2019). This is a pattern of heterogeneity broadly

consistent with (though generally even higher than) the findings in other recent meta-analyses

of cash transfers (Correa et al., 2023; Hidrobo et al., 2014; Manley, Alderman and Gentilini,

2022; Baird et al., 2013).

To probe the robustness of these results, we then estimate a series of multilevel meta-

analyses that allow us to fully account for the hierarchical structure of the data, including

multiple coefficients from evaluations of the same program in the same country. (We also

uniformly exclude outliers from this and all subsequent analysis.) Here, we find largely

consistent effects, though somewhat attenuated for income measures: $2.21 for total con-

sumption, $2.39 for food consumption, and $1.01 for income.26 We then analyze findings

from the meta-regression, where as previously noted, we present estimates only for the to-

tal consumption and food consumption outcomes, but use both the simple model and both

alternate multilevel models. The results are presented in Table 3.

In terms of the effects of intervention context, in general the pattern of evidence is not

consistent across specifications, particularly across estimates based on total consumption

versus food consumption. There is some weak evidence that the effects of cash transfers may

be larger in fragile and conflict-affected areas but this pattern is variable and is statistically

significant only at the ten percent level. There is more consistent evidence that the effects

are smaller in sub-Saharan Africa, where the coefficients of interest are uniformly negative

but vary in magnitude and precision and are statistically significant only for total consump-

tion. The magnitude of the expected decrease in effectiveness is also large and statistically

significant, implying that, on average, the expected total consumption effect size is $1.87
lower in interventions conducted in African countries compared to interventions conducted

elsewhere. Considering the adjusted expected effect size of $6.06 for the hypothetical base

category (a non-CCT, non-lump sum, and non-cash plus livelihoods intervention conducted

in a non-fragile non-African country, implemented by a non-government entity, and evalu-

ated using non-RCT or RD designs), this translates into a 31 % reduction in expected effect

size for interventions taking place in Africa.

If we evaluate the characteristics of the transfer: there is again some mixed evidence of

reduced effectiveness of transfers implemented by governments, particularly for total con-

sumption. Again considering the base category, the coefficients imply a decline of 38% and

45%, but do not hold when we look at food consumption. There is no evidence of any differ-

26If we estimate the multilevel model accounting only for dependence within multiple arms analyzed
within the same paper, again the estimates are relatively stable: $2.17 for total consumption, $2.51 for food
consumption, and $0.89 for total income.

17



ential effects of conditional cash transfers. The same specifications also show a reduced effect

of a lump-sum transfer on consumption, consistent with existing evidence in the literature

that transfers disbursed as lump sums have reduced effects on consumption, and again the

effect is large, around 71–74%. The most consistent pattern is the increased positive effect

of cash plus programs, consistently positive and significant and suggesting an increase in the

effects of cash transfers between $2 and $6, or a 46%–66% increase in the expected effect

size.

The final two variables capture the study design. Here, there is no evidence of any

differential effect size in studies conducted as randomized controlled trials in comparison

to the omitted category (dif-in-dif and matching designs). There, however, is a consistent

pattern of reduced effect sizes in regression discontinuity studies, consistent with the general

intuition that RD designs capture a local treatment effect around the discontinuity exploited

in the RD, and the effects of transfers are thus considerably smaller for that less-poor sample

close to the discontinuity. Compared to the mean effect size in the base category, the expected

impacts trend toward zero in evaluations based on an RD design. This also suggests that,

in general, meta-analyses drawing only on randomized controlled trials are likely to generate

more optimistic estimates around the effects of cash.

To sum up, our analysis suggests that cash transfers lead to precisely estimated positive

effects on consumption and income, with the estimated magnitude ranging between $1.50
and $2 in monthly income and consumption for each cumulative $100 transferred. The

effect on labor force participation is positive but extremely small and thus not meaningful

in economic terms. For the median transfer in the sample ($850), this implies a total effect

on monthly household consumption of around $13.60; for transfers at the 25th and 75th

percentiles ($424 and $1495), this implies monthly treatment effects of $6.70 and $24.22,
respectively. We will discuss the duration of these effects further below (unpacking how long

an increase in consumption plausibly persists), but as a simple descriptive point the average

duration of a cash transfer observed in our sample is 19 months.

Meta-regression analysis allows us to assess what characteristics are predictive of increases

in consumption of varying sizes, though we should note that this variation is subject to

different interpretations. A lower effect on consumption could be interpreted as higher

leakage (a lower transfer actually received, conditional on the same program target); or

reduced returns on any part of the transfer that is saved or invested (such that over time,

the additional consumption stemming from that investment is smaller in magnitude). It

would also be possible to interpret a reduced effect on consumption as corresponding to a

18



larger increase in savings that has yet to generate a positive return, but will in future, though

it is not clear how plausible a hypothesis this is for households living close to subsistence.

With these caveats, the findings suggest that while there is some variation across different

contexts, in general the effects of cash and related interventions on consumption and food

consumption of cash transfers are meaningfully smaller in sub-Saharan Africa; and meaning-

fully larger for cash plus programs. The former pattern has not been documented to date in

the cash meta-analytic literature, but the latter is broadly consistent with the evidence in

Kondylis and Loeser (2021) of larger effects of graduation programs, the primary difference

being that our definition of cash plus is broader than only graduation programs.27

There is also some weak evidence that the effects on consumption may be smaller for

lump-sum transfers, a finding consistent with (Haushofer and Shapiro, 2016), or for transfers

implemented by governments, in line with the meta-analysis findings reported by Vivalt

(2020). The reduced treatment effects observed for government programs is also consistent

with a number of analyses comparing government versus NGO performance in more specific

sectors Bold et al. (2018); Cameron, Olivia and Shah (2019); Fitch-Fleischmann and Kresch

(2021); Henderson and Lee (2015); Mo et al. (2020); however, it is notable that this effect

extends even to the disbursement of cash, an intervention that is in principle relatively easy

to implement and scale (Gentilini, 2016, 2022). The estimated effects of cash transfers are

also consistently smaller when assessed using a regression discontinuity design.

3.3 Non-reporting bias and missing results

The meta-analytic literature has widely acknowledged the potential for bias when relevant

results are not reported, particularly if there is selective non-reporting based on the sign,

magnitude, or statistical significance of the estimated effects (Page, Higgins and Sterne,

2019). Our search strategy was designed to be inclusive of findings that are not published

in peer-reviewed journals, and working papers or technical reports constitute 17% of the

sample; however, some evaluations may have findings that were never disseminated publicly,

and those disseminated publicly but without a peer-reviewed publication may be less likely

to be identified in a structured search (i.e., if a working paper or presentation is provided

only on an author or university website and is not indexed in any broader database.)28

27Comparing effects across regions is also more feasible given our broader inclusion criteria, since some
regions, particularly Latin America, are primarily represented in the non-UCT sample.

28We preferentially use the term non-reporting bias rather than publication bias following the existing
literature (Page, Higgins and Sterne, 2019); and also given that our sample does include non-published
reports.

19



We follow existing recommendations to assess non-reporting bias using and the associated

Egger’s test. While the literature has highlighted a number of potential limitations of these

tests, including limited power, these challenges are most acute in small meta-analyses (those

including fewer than 10 studies) and in meta-analyses using the log odds-ratio as a summary

measure (Peters et al., 2006; Furuya-Kanamori et al., 2020; Lin et al., 2018); neither condition

applies here. For the analysis of publication bias, we again exclude the studies characterized

by outliers.

Figure 12 presents the for the four outcomes characterized by the largest sample: total

consumption, food consumption, income, and labor force participation.29 We observe sub-

stantial asymmetry in the in the first three plots consistent of substantial non-reporting bias:

effect estimates that are noisily estimated (large standard errors) are entirely concentrated

on the right side of the graph where there are large positive treatment effects, while hypo-

thetical noisily estimated and negative treatment effects are entirely absent. Unsurprisingly,

in all three cases the Egger’s test strongly rejects the null hypothesis of no non-reporting

bias (p < 0.000 for all three outcomes). Labor force participation (Figure 12d) is somewhat

more symmetric, though in this case there is some weak evidence of non-reporting bias of

positive coefficients (p = 0.062).

For consumption, we can also further assess publication bias in various subsamples: we

assess the subsamples of RCTs and non-RCTs, studies characterized by low and high risk

of bias, and evaluations of both cash only and cash plus interventions. The are provided

in Figure A16 in the Appendix, and suggest there is no evidence that non-reporting bias

is restricted to any of these subsamples; on the contrary, there is robust evidence of bias

(p < 0.000) for all six subsamples.

It is important to note that the observed pattern in which smaller trials (generating

more imprecise estimates) report treatment effects that are larger in magnitude could also

reflect underlying patterns of heterogeneity (Egger et al., 1997; Terrin et al., 2003). In

the medical literature, this can reflect a phenomenon where smaller trials are conducted

earlier or conducted with higher-risk subsamples, both associated with larger treatment

effects; however, it is not obvious that either hypothesis is plausible here, as the treatment

effect of cash has not necessarily evolved over time, and the trials reporting more imprecise

treatment effects are not concentrated in particularly poor or fragile contexts. Another

29Note we also omit from the graph a wider set of outliers, corresponding to the estimated effect sizes
above the 90th percentile; this is implemented in order to render the graph more readable, rather than
generating an extremely dense cluster of points around the mean effect size. These studies are still included
in the estimation of p-value corresponding to Egger’s test.

20



hypothesis is that the pattern reflects underlying design considerations around statistical

power, in which researchers have chosen to conduct smaller trials precisely when large effects

are expected: however, the asymmetry is so pronounced that it is challenging to believe that

this fully explains the observed pattern. Rather, an alternate hypothesis would be that a

larger set of underpowered studies were conducted, generating a more symmetric distribution

of imprecisely estimated positive and negative coefficients, but only the former were reported.

We also draw on more recent methods employed by Brodeur, Cook and Heyes (2020) to

assess both publication bias and p-hacking in the published empirical economics literature;

here, we present simple graphs of the t-statistics for the primary effect estimates extracted in

this meta-analysis. (We focus here on the effect estimates for consumption and income and

exclude labor force participation, given that there was no meaningful evidence of publication

bias in the funnel plot). These graphs are reported in Figure A16a and show evidence

of a clear trough to the left of the line indicating significance at the ten percent level (t-

statistic of 1.64), suggestive of effect estimates that are either missing or have been p-hacked.

Interestingly, the pattern appears almost identical for the subsample of randomized controlled

trials as presented in Figure A16b – a finding that is notably different from Brodeur, Cook

and Heyes (2020), who find little evidence of bias in a much broader sample of published

RCTs. Given that this analysis draws on roughly 200 coefficient estimates (compared to

thousands in the preceding analysis conducted by Brodeur, Cook and Heyes (2020)), we

generally do not have sufficient precision to conduct the more detailed tests of p-hacking

reported by those authors, but the broad pattern is suggestive, and potentially troubling.

Insofar as this literature is characterized by biased patterns of non-reporting and p-hacking,

the estimates of the effects of cash may be meaningfully overestimated, though the magnitude

of this overestimation requires further exploration.

4 Discussion

In this section, we provide some further guidance to assess the magnitude of the primary

estimated effects and what they imply for the total effects of cash and the persistence of

these effects. We then return to the original conceptual framework to discuss some of the

reasons why the direct consumption effects of cash may be lower than the original transfer

disbursed; and describe the implications of this analysis for policymakers seeking to design

cash transfer programs to close the poverty gap in low- and middle-income countries.

21



4.1 Benchmarking the total consumption effect

In our main analysis, we meta-analyze a treatment effect that captures the effect of the

total transfer disbursed (normalized to $100) on monthly household consumption. As noted

above, we are analyzing the effect of a stock on a flow measure of consumption. This implies

two obvious follow-up questions: how does the effect of the transfer on consumption evolve

over time, and what is the accumulated effect on consumption over the full horizon in which

the transfer plausibly shifts consumption. While we can provide only very partial answers

to both questions, exploring this evidence may prove very useful.

As previously noted, around half of the evaluations in this sample are analyzing ongoing

cash transfer programs. To assess whether estimated treatment effects vary for programs

that are ongoing versus those that are completed, we pool both total consumption and

food consumption (to increase power) and estimate the treatment effect for ongoing and

completed cash transfer programs. Again using the multilevel model that pools multiple

treatment effects for the same program, our estimate suggests an effect of $2.54 during the

program period and $3.40 during the post-program period.30 Interpreting this evidence

cautiously, we would suggest that the weight of evidence suggests a consistent (i.e., non-

decreasing) positive effect of cash transfers during the transfer implementation period and

the post period observed in a typical evaluation. Again, the median trial reporting on a

non-ongoing program evaluates data collected only 13 months following the last transfer

payment, and thus should be interpreted as a relatively short-term follow-up.31

As previously noted, if we assume that the treatment effect on household consumption is

constant over the program period (median 19 months) and the post-program period (median

13 months), that implies the roughly $1.50-$2 monthly increase in household consumption

persists for around 32 months for a total, accumulated effect of consumption in the range of

$50-$60. We can then further develop this estimate, varying along four dimensions. First,

we vary the main estimated treatment effect; given the previously presented evidence that

the main program modality that generated meaningfully different effects was cash plus liveli-

hoods programming, we estimate the separate meta-analytic treatment effect on consumption

for all cash modalities excluding cash plus livelihoods ($1.33), and for cash plus livelihoods

30If we estimate the corresponding treatment effects separately for total and food consumption, the patterns
are distinct: the effect on total consumption appears higher in the post-program period, while the effect on
food consumption disappears in the post-program period.

31Note that this pattern is in contrast to the evidence presented in (Crosta et al., 2024), who find that the
effects of transfers attenuate by around 40% in the post-program period: we can replicate this pattern in
the subsample of studies that are reporting on RCTs of UCTs only, but find a somewhat different pattern
in our broader sample.

22



programming ($8.37).32 We also use as an indicative estimate the pooled effect of cash plus

livelihoods excluding treatment effect estimates above the 90th percentile in the full sample

(i.e., using a more stringent criteria to identify outliers). Bearing in mind the scope for

overestimation driven by publication bias, this third estimate ($1.88) may also be a useful

proxy for a lower estimate of the effects of cash plus livelihoods programming that corrects

for this potential bias.

Second, we vary the implied program duration during which the cash effects are observed,

using the 25th, 50th, and 75th sample percentiles of six, 19, and 24 months respectively

(and in all cases assuming, in addition, a 13-month post-program period in which treatment

effects are fully consistent, matching the median follow-up period of the evaluations in our

sample).33 Third, we vary the longer-term persistence of these effects: though we cannot

directly substantiate in this analysis persistence of cash effects beyond the typical follow-

up period, further persistence is possible, and we consider three alternate scenarios: no

persistent effects beyond 13 months post-program, effects that decay at an (annual) rate of

75% out to a five year horizon, and effects that decay at an (annual) rate of 50% out to a five

year horizon.34 Fourth, we explore alternate assumptions around discounting: no discounting

of future program effects vis-a-vis a discount rate of 5% following the first program year.

The estimates for the total accumulated treatment effect on consumption under these

various scenarios are reported in Table A6. Panel A reports the effects for cash only or cash

primarily interventions (excluding cash plus livelihoods interventions). There is considerable

variation in this panel, but the majority of the estimates are between $40 and $70, and thus

the weight of evidence seems to suggest that the accumulated positive effect of a $100 transfer
on household consumption is somewhat lower than $100; the only of assumptions that yield

an effect similar to the original transfer amount are those postulating high persistence of

treatment effects over a long period and no discounting of future treatment effects.

The estimates for the total accumulated treatment effect on consumption for cash plus

livelihoods interventions are reported in Panels B and C for the meta-analytic treatment

32Both estimates exclude outliers.
33This set of assumptions will generate a mechanical pattern in which programs assumed to have a longer

duration — conditional on the same total transfer — have larger treatment effects. We do not claim that we
have strong evidence for this hypothesis and are simply presenting a range of plausible scenarios consistent
with the stylized facts around transfer timing in our sample. In addition, we would not suggest extrapolating
further to conclude that the same transfer disbursed in small installments over a period of, e.g., five years,
could have the same positive effect on consumption over this much longer period; that would be a very
optimistic interpretation, but there is no evidence for that interpretation in our findings.

34These alternate scenarios around dissipation of program effects are consistent with the scenarios analyzed
in, for example, Bossuroy et al. (2022).

23



estimate with and without outliers. Here, we see cumulative effects that are meaningfully

larger: between $200 and $600 in Panel A, and between $60 and $100 in Panel B. Accordingly,

it seems more plausible in this case that the cumulative effect of a $100 cash transfer — in

conjunction with the livelihoods-oriented supplementary programming — has an effect equal

to or greater than $100.
However, from a cost-effectiveness standpoint it is of course important to note that the

interpretation of these findings for cash plus programs is very different. The total pro-

grammatic cost of delivering $100 of cash will be somewhat larger than $100 given costs

of program administration, but in many contexts not dramatically larger. The costs of de-

livering a cash plus program inclusive of $100 cash can be considerably higher, though the

cost structure of cash plus programs, needless to say, varies greatly, and cost information is

rarely available. To cite a limited number of examples, the graduation models in the orig-

inal Banerjee et al. (2015) paper report costs per beneficiary of between $1000 and $2000,
including a total transfer value of $500 to $1000; a more recent, psychosocial-oriented grad-

uation model implemented in Niger and analyzed in Bossuroy et al. (2022) reports costs

per beneficiary household of between $530 and $650, all in PPP terms, including $320 of

transfer value. Sedlmayr, Shah and Sulaiman (2020) present detailed cost information for a

relatively lighter cash plus intervention encompassing savings groups and training (similar to

a graduation model) that has an estimated cost of $215 per beneficiary household in Uganda

(of which around $80 is cash transfers). In just these three examples, the total cost of the

programming inclusive of cash plus is around double the value of the cash transfer itself,

implying that for the program to be cost-effective, the effects on consumption of the $100
transfer plus supplementary intervention should be at least $200. Generalizing very broadly,

the estimates of cumulative consumption benefits derived from this meta-analysis are sugges-

tive of this level of benefits using the higher treatment effect (inclusive of treatment outliers,

as reported in Panel B) but not when using the lower treatment effect.

4.2 Understanding the total effects on consumption

In assessing the reasons why the total treatment effect of cash transfers on consumption may

plausibly be lower than the original amount transferred, we can consider three potential

hypotheses: investments or savings vehicles characterized by low returns; imperfect imple-

mentation of transfers; and imperfect measurement of consumption. We discuss each channel

in turn, highlighting that each channel is somewhat speculative.

First, as noted in our original conceptual framework, the effects of transfers on con-

24



sumption encompasses both direct effects (money transferred is consumed immediately) and

indirect effects (money transferred is saved or invested, generating some future income stream

that is directed toward consumption). Certainly, the pattern of consistent transfer effects

both during and after the transfer period is consistent with the presence of the latter channel.

However, the fact that the ultimate cumulative effect on consumption is (plausibly, though

not certainly) smaller than the original transfer amount would be suggestive of some invest-

ments made that have low returns or even negative returns. Examples of this phenomenon

could be assets purchased that fully depreciate in value due to adverse shocks (animals dying

or equipment destroyed); cash savings physically lost or stolen; or business investments that

do not yield meaningful streams of income. It is also possible that there are positive returns

that are not yet captured in our time horizon and that manifest in the long-term, though

these calculations already allow for some at least partial persistence of positive income effects

up to five years.35

A second hypothesis is that the amount of the cash transfer actually received by house-

holds is lower than what they are postulated to receive: in other words, the $100 intended

transfer is attenuated to a lower amount in terms of the realized transfer.36 In estimating

the amount of the transfer in the sample, we do preferentially use amounts reported received

by sample households, if available. These estimates would incorporate any incomplete im-

plementation (if eligible households receive no transfer or a lower transfer than designed),

but these estimates are rarely available, and simpler reports on coverage (providing an esti-

mate of the number of eligible households who receive transfers) are also not available in all

papers.37

In general, the analysis assumes that eligible beneficiaries receive the full amount of

the transfer they are entitled to given the statutory program structure, and for some cash

35For example, Gertler, Martinez and Rubio-Codina (2012) document meaningful positive effects of PRO-
GRESA on household investments also yielding positive effects on income over a time horizon up to nine
years (though in this case, households can also continue to receive transfers for this entire period). Clearly,
investments generating positive returns over such a long period would imply a very different profile of cu-
mulative benefits; but there is no robust evidence suggesting that such a long period of persistent effects is
a typical trajectory.

36As noted above, we meta-analyze intent-to-treat effects given that the probability of high spillovers,
either positive or negative, for cash transfers renders treatment-on-the treated estimates arguably somewhat
implausible.

37The appropriate definition of this concept also varies depending on the empirical design: many papers
engage in some comparison of households eligible for transfers versus households ineligible for transfers, but
some—particularly non-experimental or matching designs—may be focused on a treatment sample that is
defined by realized payment status, rather than eligibility, in which case there is little scope for attenuation
due to implementation errors.

25



transfer programs (particularly those implemented by non-governmental organizations and

those implemented at a smaller scale), this may be a plausible assumption. For example,

Haushofer and Shapiro (2016) reports that around 85% of eligible households receive transfers

in programming rolled out by GiveDirectly; Premand and Barry (2022), reports that 98%

of target households receive cash transfers in a government cash transfer program in Niger.

However, some transfer programs are characterized by much lower coverage (much higher

rates of non-compliance): for example, Briaux et al. (2020) reports that in an unconditional

cash transfer program implemented in Togo, 58% of target beneficiaries never received any

cash. Some long-running government transfer programs such as the child support grant

in South Africa have been initially characterized by relatively low coverage rates that have

shifted over time (Case, Hosegood and Lund, 2005; Heinrich and Brill, 2015). Quantitatively

summarizing this evidence is extremely challenging, but it is clear that at least in some

contexts, low coverage rates for eligible households imply that our constructed estimate of

transfer magnitude may be an overestimate.

A third hypothesis is that the effects on consumption, broadly defined, are in fact larger

than those captured in typical evaluations of cash transfer effects and that some key cate-

gories of cash transfer expenditure are missing. One potential category is expenditure on

housing: this is an extremely popular form of investment, particularly for larger lump-sum

transfers (see for example Haushofer and Shapiro (2016)). However, its inclusion in con-

sumption aggregates is problematic, requiring analysts to consider the flow of utility the

household receives from occupying its dwelling within a given reference period instead of the

total purchase value in the same period (Deaton and Zaidi, 2002). In practice, this requires

using actual or imputed rents, but there is no consistent approach to imputing rents for non-

rental households and, as a result, housing-related expenditures are often not considered at

all in standard consumption aggregates (Mancini and Vecchi, 2022).

A second potential category is transfers to other households, particularly if cash transfers

are incorporated into systems of informal insurance. Again, this type of expenditure would

not typically be included in standard consumption aggregates for fear of double-counting if

the same transfers would show up in the consumption of other households (Deaton and Zaidi,

2002). Available evidence about positive spillover effects of cash transfers has documented

the salience of interhousehold transfers or gifts in generating positive spillovers in some

contexts (Angelucci and De Giorgi, 2009) though not in others (Egger et al., 2022). It is also

possible that transfers flowing into the household (remittances or other forms of informal

insurance) decrease in response to receipt of a cash transfer, reducing the positive effect on

26



consumption.

4.3 Evaluating transfers required for exit from poverty

Using our estimates of transfer effects on consumption, we also aim to evaluate the size of

the (cumulative) transfer required to move households in poverty above the poverty line in a

range of lower- and middle-income country households. One of the main goals of cash transfer

programs is poverty alleviation; accordingly, the analysis in this section seeks to understand

what these estimates imply for policymakers and donors regarding the magnitude of the

transfer required to achieve this goal.

This analysis involves three steps: first, we use estimates of the poverty gap for a ma-

jority of countries in the sample from the World Bank’s Poverty and Inequality Platform or

PIP(World Bank, 2022)38 to identify the magnitude of the increase in individual consumption

required to exit poverty. Second, we use the poverty gap in conjunction with data on house-

hold size (from the studies included in our sample) to estimate the household-level monthly

poverty gap in absolute terms: i.e., the amount of additional consumption a household would

have to report each month in order to exit poverty.39 Third, we use our meta-analytic esti-

mates of the average effect of cash transfers on consumption (excluding outliers, $1.62 per

$100 transferred, as reported in Table 2) to calculate the size of the cumulative transfer

required to generate an exit from poverty. For poverty gap estimates, we use the most recent

data year available for each country, with the objective of estimating the size of transfers

that would be required currently; however, we express this data on poverty gaps using the

2011 PPP dollars and 2011 poverty line ($1.90), as this year is closest to the PPP year em-

ployed in the remainder of our analysis (2010).40 As discussed in detail previously, while it is

challenging to be precise about the duration of the positive effect on consumption generated

by these transfers, the weight of evidence generally suggests that within our sample, the

effect persists for around 2.75 years (inclusive of the period of program implementation).

The estimated value for the transfer required for each country is reported in Column (5)

of Table A7. There is considerable variation in these estimates due to large differences in

38We used the user-written Stata command pip (Castaneda, 2023) to compute the poverty gap estimates.
For more details about the PIP, see: https://pip.worldbank.org/about.

39If we have multiple studies in the sample reporting household size for a particular country, we calculate
the average.

40However, for some countries, the latest available data preceded 2000, and these countries were excluded
from this analysis. Afghanistan and Somalia have no PIP data available. We also exclude sample countries
that are characterized by a poverty gap of zero or near-zero, and those with no studies in our sample where
household sizes are reported.

27

https://pip.worldbank.org/about


poverty gap estimates and reported household size across the countries in our sample; the

cumulative transfer required for Zambia, for example, is $5950, while for Bangladesh where

the average household is closer to the poverty line and has fewer members, the required

transfer estimate is only $149. Again, this is a cumulative transfer amount; the typical

intervention in our sample has a duration of 19 months with monthly or bimonthly transfers.

Column (6) shows the average monthly transfer required in 2011 PPP terms for two years;

this is around $300 monthly for Zambia and only around $8 for Bangladesh. For comparison,

Table A7 also reports the 2010 PPP-adjusted cumulative dollar value of the average transfer

within that country observed in our sample (in Column (3). It is important to note that in

many cases, these transfer programs were implemented at least 10 years ago (and in Latin

America, the time gap is usually at least 20 years). Given that extreme poverty has been

generally declining over time and in some cases quite rapidly, comparing the past transfer

to the current required transfer is only an indicative exercise.

With that caveat, however, we observe that in general for countries in Latin America and

Asia, the transfers implemented and evaluated in our sample are in fact significantly larger

than the estimated transfer required to lift a typical poor household out of extreme poverty

given the most recent available data (the only exception is Honduras).41 This may partly

reflect the fact that the extreme poverty line is no longer a particularly relevant benchmark

for these less poor or middle income countries, and in fact the national poverty line generally

increases with country income level.42

However, in sub-Saharan Africa, exactly the opposite pattern is observed: the cumulative

transfer required to generate a household exit from poverty is meaningfully larger than the

transfers observed in this sample, and this is true for every country site excluding only South

Africa and Zimbabwe.43 In Ghana, Malawi, and Togo, the required transfer is around 7–7.5

times larger than the average transfer observed; in Kenya, Liberia, Lesotho, and Rwanda,

around 2.5 times larger; and in Niger, Nigeria, and Uganda around 3.6–4 times larger. 44 The

highest estimated required trnasfers are in Malawi and Zambia, where the monthly transfer

41In the case of Latin America, this is partly because the cash transfer programs evaluated are generally
long-running CCTs in which households have a lengthy period of eligibility, and thus the cumulative transfer
estimate is large.

42See for example Ferriera et al., “ A richer array of international poverty lines”:
https://blogs.worldbank.org/en/developmenttalk/richer-array-international-poverty-lines

43In South Africa, the high estimated cumulative transfer value again reflects the long-running character-
istics of the child grant program.

44Note that this is assuming a consistent effect of cash transfers in all contexts; it is also the case that
there was some evidence that cash transfer had reduced effects in sub-Saharan Africa, suggesting an even
larger transfer would be required.

28



amount required to lift a household out of poverty reaches $270–300. We argue this exercise

is useful in understanding the magnitude of cash transfers required to generate household

exit from poverty, how it compares to current transfer amounts, and regional variation,

highlighting that in sub-Saharan Africa in particular, the magnitude of current cash transfer

programs is significantly lower than the transfer size required to shift households out of

poverty.

5 Conclusion

We have presented a systematic review and meta-analysis around the effects of cash transfer

and cash plus programs on livelihoods outcomes across a range of contexts. Our findings

suggest that cash transfers generate robust positive effects on household consumption and

income but no significant shifts in labor force participation. These positive effects are sig-

nificantly larger for cash plus programs. We also present indicative evidence around the

cumulative effects on consumption of cash transfer programs under a range of scenarios, and

compare the transfers observed to the transfers required to generate an exit from poverty in

a number of sample countries.

29



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