metadata: authors: 0: author: Aguilar,Arturo
1: author: Barnard,Cristina
2: author: De Giorgi,Giacomo
count: Mexico
docna: 0: docna: Long-Term Effects of PROSPERA on Welfare
docty: Policy Research Working Paper
subtopic: Health Care Services Industry,Educational Sciences,Inequality,Disability,Access of Poor to Social Services,Economic Assistance,Services & Transfers to Poor,Labor Markets
teratopic: Industry,Social Protections and Labor,Education,Macroeconomics and Economic Growth,Poverty Reduction
abstracts: cdata!: The long-term effects of Mexico's
            conditional cash transfer program, PROSPERA, on poor
            households are of great interest to policy makers and
            academics alike. This paper analyzes the long-term effects
            on the welfare of the original participant households and
            their offspring, about 20 years after the inception of the
            program. To complement other studies that look into the
            effects on schooling and health, the analysis focuses on a
            utilitarian definition of welfare and employs two empirical
            strategies. The first uses the 1997-2000 experiment as the
            cleanest, albeit limited, source of variation. The analysis
            finds that by 2017–18, the offspring of original beneficiary
            households are more likely to have formed their own
            households, to have migrated to different localities, and to
            have more durable assets and larger consumption expenditures
            than their control counterpart. The second strategy confirms
            and expands those findings using a difference-in-difference
            methodology based on the localities' rollout of the
            program and the age of the individuals, as a proxy of
            exposure. This second approach covers a much larger and
            representative sample, while also directly observing
            self-reported vulnerability in food consumption. The
            findings confirm the generally positive outlook in terms of
            durable assets and lower food vulnerability. Perhaps more
            interestingly and relevant for evaluating the success of the
            program is that it improved intergenerational mobility.
            Using the 1997-2000 experiment, the analysis finds that the
            young adults who benefited from the program improved with
            respect to their parents in education, assets holding, and
            income. They appear to be climbing the ladder of assets and income.
geo_reg_key: 119228,517191
alt_title: 0: alt_title: Efectos a largo plazo de PROSPERA en el Bienestar
repnme: repnme: Long-Term Effects of PROSPERA on Welfare
display_title: Long-Term Effects of PROSPERA on Welfare
listing_relative_url: /research/2019/09/31393945/long-term-effects-prospera-welfare
topicv3: Poverty m1326687 695,Education m1327048 470,Cash Transfers m1327437 1608,Jobs m1503931 2670,Health m1504661 3480
publishtoextweb_dt: 2019-09-09T00:00:00Z
historic_topic: Industry,Social Protections and Labor,Education,Macroeconomics and Economic Growth,Poverty Reduction
no_of_pages: 46
author_keys: 0: author_key: 1278359
fullavailablein: node_id: 31393945
model_extractions: Policy Research Working Paper 9002 Long-Term Effects of PROSPERA on Welfare _Arturo Aguilar Cristina Barnard Giacomo De Giorgi_ Social Protection and Jobs Global Practice September 2019
Policy Research Working Paper 9002

# **Abstract**

The long-term effects of Mexico’s conditional cash transfer program, PROSPERA, on poor households are of great interest to policy makers and academics alike. This paper analyzes the long-term effects on the welfare of the original participant households and their offspring, about 20 years after the inception of the program. To complement other studies that look into the effects on schooling and health, the analysis focuses on a utilitarian definition of welfare and employs two empirical strategies. The first uses the 1997– 2000 experiment as the cleanest, albeit limited, source of variation. The analysis finds that by 2017–18, the offspring of original beneficiary households are more likely to have formed their own households, to have migrated to different localities, and to have more durable assets and larger consumption expenditures than their control counterpart.

The second strategy confirms and expands those findings using a difference-in-difference methodology based on the localities’ rollout of the program and the age of the individuals, as a proxy of exposure. This second approach covers a much larger and representative sample, while also directly observing self-reported vulnerability in food consumption. The findings confirm the generally positive outlook in terms of durable assets and lower food vulnerability. Perhaps more interestingly and relevant for evaluating the success of the program is that it improved intergenerational mobility. Using the 1997–2000 experiment, the analysis finds that the young adults who benefited from the program improved with respect to their parents in education, assets holding, and income. They appear to be climbing the ladder of assets and income.

This paper is a product of the Social Protection and Jobs Global Practice. It is part of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy discussions around the world. Policy Research Working Papers are also posted on the Web at http://www.worldbank.org/prwp. The authors may be contacted at giacomo.degiorgi@unige.ch and the coordinators of the studies may be contacted at cavilaparra@worldbank.org.

_The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent._ Produced by the Research Support Team
# Long-Term Effects of PROSPERA on Welfare<sup>_∗_</sup>

Arturo Aguilar<sup>_†_</sup> Cristina Barnard<sup>_‡_</sup> Giacomo De Giorgi<sup>_§_</sup>

## **Keywords:** PROSPERA, Social Program, long-term, Welfare. **JEL Codes:** I38, O12, O15

> _∗_ This paper is part of the research project “Studies of PROSPERA’s long-term results” which was funded by the Government of Mexico through the National Coordination of PROSPERA (CNP) as part of a technical cooperation agreement with the World Bank. The World Bank team is grateful to the Government of Mexico, including the Ministry of Social Development (now Ministry of Welfare), Ministry of Education, and Ministry of Health, for the close collaboration in this research project, including the provision of the main datasets. The World Bank team would also like to thank the National Council for the Evaluation of Social Development Policy (CONEVAL), the National Institute of Public Health, development partners such as the Inter-American Development Bank, and the national and international researchers that contributed in the Advisory Evaluation Group. This group was established to ensure technical quality and methodological rigor of the “Studies of PROSPERA’s long-term results.” These studies were coordinated by Maria Concepci ́on Steta, WB Senior Social Protection Specialist; Clemente Avila, WB Social Protection Economist; and M ́onica Orozco, WB Consultant.<sup> ́</sup>

> _†_ ITAM

> _‡_ ITAM

- _§_ GSEM-University of Geneva, MOVE, BGSE, UAB, BREAD, CEPR, IPA
# **I Introduction**

The long-term analysis of Mexico’s conditional cash transfer program (CCT), PROSPERA, constitutes a substantial resource for policy makers, and researchers alike. Mexico’s world famous CCT PROSPERA (previously named PROGRESA and Oportunidades), with its focus on human capital investment in terms of health and education, has already inspired several programs around the globe and has shaped the way researchers, policy makers, and politicians interact on the implementation and evaluation of large policies.<sup>1</sup> Moving beyond the short-term analysis will give the opportunity to understand whether the short-term impacts translate into benefits in the long run, and not only for original beneficiary households but also, and most importantly, for their offspring. This analysis is crucial since one of the main goals of the program is to break the intergenerational cycle of poverty in which parents’ conditions worked as a key barrier to their children’s success in life. This would be a tremendous accomplishment of any policy and as such deserving of the greatest attention.

In this work, we study the long-term effects of the program by providing answers to the following questions:

1. Did the program improve the long-term welfare of _participants_ ?

2. Did the program contributed to break the cycle of poverty of _participants_ and their offspring (intergenerational mobility)?

Answering these questions is not a simple task. To begin with, the concept of _welfare_ is far from being unequivocally determined.<sup>2</sup> Atkinson (2011) and Deaton (2018) recently reignited a decades-long discussion about the proper way to define and measure such an elusive concept. Sen (1970, 1973, 1986, 2006) has played a leading role in this debate by challenging an _utilitarian_ approach to welfare and rather promoting a _capabilities_ approach based on the idea that outcomes or decisions (observable to the researcher) portray an incomplete picture of the actual well-being of the individual. The ample literature studying PROSPERA’s benefits has looked into many different dimensions of an individual and household’s life covering _welfare_ from different perspectives. This paper is limited in that sense. We chose to focus on a consumption-based approach of _welfare_ , which is more in line with the _utilitarian_ view. The _utilitarian_ perspective of _welfare_ is justified by the fact that from an economics theory perspective, consumption is usually the main input in utility functions.<sup>3</sup> While we strive to employ a more comprehensive definition of _welfare_ than one based only on consumption and labor

> 1Appendix A gives a general description of the program.

> 2The references to the conceptual definition of welfare do not intend to be exhaustive. They are just intended to give a small flavor of these remarkable authors’ extensive work on the topic.

> 3For example, in the motivation for the Nobel prize awarded to Angus Deaton in 2015: _...The consumption of goods and services is a fundamental determinant of human welfare...._ https://www.nobelprize.org/nobel ~~p~~ rizes/ economic-sciences/laureates/2015/advanced-economicsciences2015.pdf.

2
supply, our analysis is complementary to other papers that are being produced as part of this set of studies, which look into education, health and occupational mobility. Also, at the time of writing, we are constrained by the data availability, while future work could include several other indicators as data become more available.

The consumption-based approach to _welfare_ used in this paper will focus mainly on ownership of durable goods, while also proposing a measure of (imputed) non-durable consumption (food, personal products, and clothing). This is justified by the fact that consumption reflects a household’s permanent income level and its resilience to shocks (Deaton and Zaidi 2002). It also reflects better than income the household’s life conditions. In fact, this explains why PROSPERA’s targeting used a proxy-means test index based on household durables and household members characteristics to identify vulnerable households to be served (Skoufias et al. 2001). Secondly, we will look into measures of success by looking into labor market outcomes of those individuals that as children were encouraged by the program to stay enrolled in school. Finally, to look into the intergenerational transmission of poverty we look into measures of mobility in the percentile rankings, as in Chetty et al. (2014) of selected outcomes. Our definition of mobility is now fairly standard in the literature and focuses on the relative position in the outcome distribution of individuals with respect to their parents. In practice this means that we order our data in ascending order on the magnitudes of the outcome of interest for parents and offspring separately, this ordering would give us a relative position in the relevant distribution. We then compare the relative position of the parents to that of the offspring. If they have exactly the same position there is no mobility across generations; if those at the bottom see their offspring climb up the ladder, we have upward mobility; and the largest mobility would be found if the position of the parents were to be unrelated to that of the offspring.

In the best case scenario, we would find that by (i) allowing families to insure against temporary shocks, (ii) lifting incomes to higher and more stable levels, and (iii) through the investment in both physical and human capital (education, and health) the program can generate a virtuous cycle. This could be reflected in the investment and improvements of outcomes for beneficiaries and their offspring, potentially lifting future generations out of poverty. We defer to future work the extensions to other aspects and approaches to _welfare_ analysis, while we already directly speak to a multifaceted strategy that includes multiple indicators (see for example Ravallion (2011)), and measures of social deprivation, as the ones suggested by the National Council for the Evaluation of Social Development Policy (CONEVAL).<sup>4</sup> The second challenge we face is methodological. We should note here that a large part of the analysis focuses on the long-term effects of the original experimental design, which is the cleanest identification strategy and source of variation in this context, but comes at a high cost. Essentially, the experimental variation gives an early versus late treatment difference. This

> 4See https://goo.gl/aQ8MPt

3
early-late dichotomy is just a little more than a year of extra transfers for the treated group, or about 9% additional resources available during the first period of the experiment as the control group began receiving transfers just after the initial experiment. This design therefore is more an intensive margin of treatment rather than an extensive one.<sup>5</sup> In a way, the estimated effects could be understood as lower bounds for the true effects out of an extensive treatment and therefore any positive effect should be taken as a success of the program given the limited variation in the available data. Importantly, we also implement an alternative research design which allows us to get closer to the treatment versus pure control exercise; in that approach we use the program sequential roll-out and individual ages to identify the effect of several years of treatment versus never directly treated status as those children older than 16 at the time of the introduction of the policy would not be directly exposed to it (or in any case to a much lesser extent as they would be unlikely to satisfy the age requirement for the conditional components).

The main effects of PROSPERA can be summarized as follows: (i) newly formed households, those of the offspring of the initial and original beneficiary households, see a substantial increase in their durable purchases in particular for entertainment and kitchen goods as well as for (imputed) non-durable consumption expenditures; (ii) original households do not appear to have a large increase in durables; and (iii) new households tend to locate in different localities than those where they lived in 1997 (usually where they were born). These results are consistent with the fact that the offspring of the original households are the direct recipients of the additional human capital both in health and education due to the program, therefore they appear to be on a different long-term development path than their control counterpart. In particular, we see that the largest effects are concentrated among those with the largest initial effects on human capital accumulation in the sample: those who were at the verge of dropping out of secondary school in 1997/98, i.e. those who were aged 11-16. We need to remind the reader that the experiment used for this part of the analysis lasted between 1998 and 1999. Hence, while it is possible that there could be large improvements in the very young children (e.g. aged 0-5 in our analysis), this would become evident in terms of assets by the time their human capital accumulation ends, which is not possible to observe in our exercise. In fact, when we look at a different data source and provide a complementary research design, in Section V.B, we find that the effects of PROSPERA are generally largest for beneficiaries affected since their developmental stages.

In terms of intergenerational and lifecycle mobility, we find that young adults who formed their own households fare substantially better than their parents in terms of schooling, assets,

> 5The _intensive margin_ refers to a comparison of receiving _more_ with respect to receiving _less_ . In contrast, the _extensive margin_ refers to a comparison of receiving an intervention with respect to not receiving it. In our context, the group that was initially defined as the _control_ , began to receive the benefits of the program in 1999. Hence, the treatment versus control comparison should be interpreted as one in which the treatment received _more_ resources (9% more transfers in total) since their enrollment to the program was _earlier_ (a little more than one year). This explains why we assume our comparison to be in the intensive margin.

4
and income when compared to their control counterparts. These latter results are very encouraging, as exactly that was the aim of the policy. A program like PROSPERA should ultimately allow the next generation to thrive and climb the ladder of society, thus breaking the cycle of poverty. Finally, to estimate the benefits of PROSPERA throughout its existence, we provide a back-of-the-envelope exercise that draws upon Gertler et al. (2012). We compute the effects on non-durable consumption expenditure for the 1997-1999 treated households compared to a control group that does not receive any transfer. Such exercise estimates an effect of about 25%, per adult equivalent, over the baseline consumption in 1997 (at 2017 prices).

The remainder of the paper includes a selected review of the literature (Section II); a description of the potential mechanisms through which the program can have long-term consequences on the lives of the original households as well as their offspring (Section III); a thorough description of the data employed (Section IV), and the empirical strategies adopted (Section V). We will then move on to the results in Section VI, and finally conclude in Section VII.

# **II Literature Review**

In order to locate the contribution of our work in the now vast literature on PROSPERA we will mention below the more relevant papers on which we build upon. It is important to mention that there are several papers analyzing the short and medium term effects of the program on different outcomes of interest for our work. It would be beyond the scope of the current paper to have a fully exhaustive list of all the publications that over the past two decades have analyzed the program, we will just focus on a selection of studies closely related to our own. Despite the large literature, very few papers have looked into the specific aspects of long-term success that we focus on, in this sense we see our work as complementary to the amount of knowledge accumulated over the years for two main aspects: i. our main focus is on welfare through a standard definition of purchasing/consumption behavior; ii. needless to say we are interested in the long-term implications of the policy not solely in terms of looking at the 20 years of outcomes, but, perhaps more important, is our interest on the next generation or the offspring of original households involved in the program since its inception.

For example, there are a number of studies on the impact of the policy on the consumption profiles of beneficiaries (Hoddinott and Skoufias 2004) and non-beneficiaries (Angelucci and De Giorgi 2009 and Angelucci et al. 2017). These studies find robust evidence of increase in consumption of non-durables (food mostly) and to a lesser extent of durables for both recipient households and other family members residing in the same locality as the direct transfer recipients. Importantly, Angelucci et al. 2017 look at whether such positive impacts persist in the medium term, defined there as six years since the initial transfers.

A more limited literature on longer term impacts of PROSPERA is available, and, in general, 5
of long-term effects studies of CCT programs. Millan et al. (2018) give a recent summary of papers investigating long-term effects of these policies. Relevant examples include: analysis on long-term effects on human capital (Barham et al. (2017) study a CCT in Nicaragua); similarly, Baez and Camacho (2011) study the long-term effects of the Colombian CCT ( _Familias en Accion_ ) on human capital; similar analyses are presented in Barrera-Osorio et al. (2017) and Aizer et al. (2016) on children’s longevity, educational attainment, nutritional status, and income in adulthood in the U.S. There is also a literature looking into different aspects of the transfers: conditional versus unconditional (Baird et al., 2011; Bursztyn and Coffman, 2012), targeted versus universal (Niehaus et al., 2013), as well as other aspects of the transfers (Haushofer and Shapiro, 2016). However, determining aspects of the transfers is beyond the focus of our analysis.

For the case of Progresa/Oportunidades/PROSPERA, Behrman et al. (2011), Gertler et al. (2012) and Angelucci et al. (2017) look at the medium-term effects on consumption, human capital, and investment behavior. Later, Kugler and Rojas (2018) investigate the long-term effects on human capital and labor market outcomes for the original experimental population. Also recently Parker and Vogl (2018) focus on the children of original beneficiary households and find positive effects on human capital, assets, housing and labor market outcomes. Finally, Adhvaryu et al. (2018) study how PROSPERA protected children from early life shocks, helping them escape from potentially long-term adverse shocks.

# **III Potential Mechanisms**

There are potentially many channels through which PROSPERA might change the lives of beneficiaries, and non-beneficiaries alike. This section is meant to present a stylized theory of change rather than a detailed account of the possible mechanisms through which PROSPERA might have long-term effects. There are potentially many such channels, which depend on whether one looks at the original beneficiary households or their offspring, so that a detailed account would be beyond the scope of this paper. However, we will build upon other authors’ work to motivate our own approach and analyze our results.

As is well known, the program was designed to tackle multiple aspects of poverty and how to escape it. In particular, the program targeted education, health, and nutrition through transfers and conditionalities. It is therefore immediate to think that for the children of the original households a direct virtuous channel going through the accumulation of human capital should exist. A larger human capital would then improve the livelihoods for the treated in a stable manner. The children of the original beneficiaries are by 2017/8 adults themselves, and given the higher schooling and better health they can be more productive and earn higher incomes. Such higher permanent incomes, and human capital, would then translate into better living standards. We will confirm here that indeed PROSPERA increased the human capital, in terms of school6
ing, and health of the children of the original households. There are, however, other important potential channels from i. asset accumulation, to ii. occupation, and iii. entrepreneurship. There is by now plenty of evidence on the positive effects on educational and health outcomes (Todd and Wolpin 2006; Angelucci et al. 2010; Bobonis 2009; Lalive and Cattaneo 2009; Attanasio et al. 2012; Parker and Vogl 2018) for both beneficiaries and non-beneficiaries. Also, evidence has been shown about occupational choices and investment behavior (Bianchi and Bobba 2010; Gertler et al. 2012; Angelucci et al. 2017). In addition, the program has proven effects on occupational mobility (Yaschine 2012), and female empowerment and household decision processes (Attanasio and Lechene 2002, Attanasio and Lechene 2014, Bobonis et al. 2015). All this literature asserts that the original households’ members are more educated, and appear to have accumulated more productive assets, as well as initiated productive business activities. The general consensus emerging from the literature is that PROSPERA has achieved substantial improvements in the short to medium term as a result of higher human capital, more stable income flows, and profitable investment into assets and occupations.

We build on all this existing evidence to make the case for the long-term and intergenerational effects on our main measures of well being. In general, savings and therefore investment can rise due to a larger disposable income and reduced general uncertainty for beneficiary households. Higher incomes can afford previously unattainable investments, while lower uncertainty in terms of future income streams lowers the need for precautionary or unproductive savings, while allowing households to take more risk into business ventures (Banerjee and Duflo, 2011). Similarly, better educated individuals might be making better long-term consumption decisions. Previously severely credit constrained beneficiary households can now start saving and investing for the long-term and their offspring.

We acknowledge that all these channels, or more, could be in operation at once. Even though we will discuss some channels when relevant, attempting to decompose the overall effects on each channel is not the purpose of the present study. Rather, we focus on estimating the overall policy effect of the program on different measures that reflect higher wellbeing. Doing so is empirically challenging given that original experiment variation provides only a small window of differential exposure. Two aspects of such differential exposure will be exploited in our analysis: first, the fact that households in experimental localities receive a larger aggregate amount and time exposure to resources. Second, in parts of the analysis we will pair this with cohort variation, which gives differential exposure at critical stages. Two meaningful examples are: educational stages in which high levels of dropouts are frequent (especially among poor recipients) and critical early developmental stages. For both cases, the literature on the program has already provided favorable evidence.

7
# **IV Data**

We employ two data sources for the analysis presented here: (1) the PROSPERA panel data gathered, since 1997 all the way to 2017-2018 (on a subset of localities and individuals), for the evaluation of the initial experiment and (ii) the 2015 intercensus data collected by the National Institute of Statistics and Geography (INEGI).

## **IV.A PROSPERA ENCEL panel**

As it is widely known, in 1997 a sample of 24,077 households in 506 rural localities was selected to implement a randomized controlled trial (RCT) in order to give robust evidence about the effects of PROSPERA (known as Progresa at that time).<sup>6</sup> This set of localities, chosen according to the administration of the program guidelines, where then allocated to a treatment (320 localities) and a control group (186 localities) where the eligible households in treatment group received PROSPERA’s support, transfers were distributed to those eligible households who complied with the stated rules of the program, starting in the fall of 1998 while the control localities started to receive the same treatment at the very end of 1999. Such sample was followed up with a survey instrument called ENCEL in 1998, 1999, 2000, 2003 and 2007 to give evidence of short and medium-run impacts of the program. In an effort to provide relevant data to evaluate the effects of PROSPERA in the long-run, the World Bank, PROSPERA and the National Institute of Public Health (INSP) partnered to gather information in 2017-2018 on a subset of that sample of participants.

**ENCEL 2017-2018 sampling framework.** Given the budgetary restrictions and the complexity of tracking back the original participants, which was the strategy of the previous rounds of the panel, a sub-sample of 334 localities of the 506 original localities was selected.<sup>7</sup> As Panel A in Table 1 shows, this first filter meant that richer eligible households in less marginalized localities would become the sample target. Each of the selected localities was visited and the surveyors looked for the 18,564 households included in the 1997 sample that inhabited that locality. The targeting strategy employed at the beginning of the program to select beneficiaries defined 12,519 of these households as eligible. We will focus our analysis in this set of households, since they provide the variation that would be relevant for the analysis.<sup>8</sup> Priority was given to households that had young members at the start of the data collection (1997-2000). In total, 7,824 eligible households were located in the 2017-18 data collection. Hereon, we

> 6At the beginning of the program, priority was given to rural localities. In Mexico, rural localities are defined as those with fewer than 2,500 inhabitants.

> 7Localities that were more accessible and as a result richer within the 506 original full sample were selected for the ENCEL 2017-18. A set of localities that were added in the 2003 round are not included in the sampling framework for the 2017-18 round.

> 8Non-eligible households could have enrolled later to the program. However, comparing non-eligible households from treatment and control communities would involve selecting households that initially did not receive the program and were not affected by the random allocation of treatment.

8
will refer to them as the **original households** , since their sampling took place back in 1997. Panel B in Table 1, shows the attrition resulting from the inability to locate some of the original households in the 334 selected localities. Larger households with more assets are more likely to be surveyed in 2017. Importantly, and central for the internal validity of the estimated effects, we show that the overall attrition described appears orthogonal to treatment (see _Table 2_ ). This latter result is reassuring in terms of causal identification of the treatments effects, however we should mention that those effects might not be applicable to the entire population of interest. Despite that concern we conjecture that the sampling framework adopted is likely to produce underestimates or conservative estimates of the effects as the sample, includes better off households to start with, and it is plausible that the program effects would be smaller for those households.

Next, using a list of all the individuals in the 1997 original households, surveyors asked for socio-demographic information about each of them, as well as for the new members living in the household (these would be offspring or other individuals entering the household after the 1997 survey round). Among the original set of individuals, a separate survey was designed for members that were in critical age groups at the time in which the program started. Three age groups of interest were then defined: (i) newborns in 1997-2000, since they were in a critical stage of development when the RCT took place; (ii) children 6 to 8 years old in 1997-2000, since they were about to enroll in school grades where the program’s conditionalities are most relevant; and (iii) children in sixth grade in 1997-2000, since the program’s positive effects in terms of later school enrollment appear to be concentrated in this critical grade.

Importantly, these individuals could be still living in the _original households_ , but they could have also moved out to form a new household (or joined an existing one). Contact information was recorded to track these individuals. This search process had a geographic limitation: interviews with individuals that moved out of the original household were only attempted if they settled in the same locality as the original household, within a short range of the original household’s locality<sup>9</sup> or in the three main metropolitan areas in Mexico (Mexico City, Monterrey and Guadalajara). As mentioned above, the households where these individuals were located could be either newly formed households (e.g. the individuals married or just decided to move out by themselves) or could be households that already existed and the individual decided to move in (e.g. moving with relatives). For the purpose of our analysis we define all these households as **new households** in the sense that they did not exist in the 1997 sample.

Surveyors were able to locate and interview 4,987 individuals in the relevant group ages: 2,105 of them were still in their original households and the remaining 2,882 were in new households. Of the individuals living in a new household, 4,207 interviews were not successfully completed, either because they moved to a household not accessible given the survey 9Given budgetary restrictions, households were searched in localities located within a 30 minute driving distance at most.

9
|**ition**<br>p-values|0.0000<br>0.0000<br>0.0000|0.1872<br>0.0000|0.0000<br>0.0000<br>0.0904<br>0.0000<br>0.0000<br>0.0000<br>0.0000<br>0.0000<br>0.0000<br>0.0309<br>**.0000**<br>riginal households<br>t the locality level.|
|---|---|---|---|
|**ctive attr**<br>Diff|-0.0462<br>-3.3737<br>0.3447|0.1206<br>-0.2233|-0.0553<br>0.0932<br>0.0071<br>0.0843<br>0.0738<br>1.6423<br>0.7885<br>0.6830<br>-0.0563<br>-0.0809<br>**value**_<_**0**<br>fnd the o<br>lustered a|
|**sponse sele**<br>Sample|0.0579<br>40.3251<br>2.9477|1.7628<br>4.8391|0.7066<br>0.6612<br>0.0456<br>0.3504<br>0.3707<br>6.8556<br>2.1057<br>2.1471<br>0.0701<br>0.5833<br>4,494<br>**= 80.04 p-**<br>apability to<br>ard errors c|
|**Panel B: Re**<br>Mean<br>Non-respondents|0.1040<br>43.6988<br>2.6030|1.6422<br>5.0624|0.7619<br>0.5680<br>0.0385<br>0.2661<br>0.2970<br>5.2133<br>1.3172<br>1.4641<br>0.1264<br>0.6643<br>5,307<br>**Joint test: F-stat**<br>t the sample and the c<br>NCASEH data. Stand|
|**rition**<br>p-values|0.3419<br>0.0447<br>0.2534|0.5711<br>0.0706|0.2382<br>0.0066<br>0.3416<br>0.2921<br>0.4476<br>0.0006<br>0.0090<br>0.0041<br>0.0020<br>0.2985<br>**8**<br>hed to selec<br>the 1997 E|
|**selective att**<br> <br>Diff|-0.0069<br>-1.0319<br>0.1520|-0.0906<br>-0.0758|-0.0296<br>0.1252<br>0.0093<br>0.0285<br>-0.0180<br>0.2699<br>0.1188<br>0.1213<br>-0.0308<br>-0.0957<br>**value = 0.12**<br>tion establis<br>culated with|
|**eographical**<br>an<br>Localities in|0.0828<br>42.1468<br>2.7620|1.6975<br>4.9582|0.7365<br>0.6107<br>0.0417<br>0.3048<br>0.3308<br>5.9663<br>1.6790<br>1.7773<br>0.1006<br>0.6272<br>9,801<br>**tat = 2.02; p-**<br>raphical restric<br>shown are cal<br>*10%level.|
|**Panel A: G**<br>Me<br>Localities out|0.0898<br>43.1787<br>2.6100|1.7881<br>5.0339|0.7661<br>0.4855<br>0.0324<br>0.2762<br>0.3488<br>5.6965<br>1.5602<br>1.6560<br>0.1314<br>0.7229<br>2,718<br>**Joint test: F-s**<br>sed on the geog<br>ce of variables<br>1%, **5%, and|
||**aracteristics**|**tive activities**<br>ome PC)|**s and assets**<br>ship*<br>**aphics**<br>**ristics**<br>tion index 1995<br>ective attrition ba<br>EH sample. Balan<br>fcance at the ***|
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10
<u>Table 2: Balance table.</u>

||M|ean|||
|---|---|---|---|---|
|1997 Variables|Control|Treatment|Diff|p-value|
|**Household head characteristi**|**cs**||||
|Female*|0.0571|0.0583|0.0012|0.8868|
|Age|40.5610|40.1865|-0.3745|0.4146|
|Years of schooling|2.8088|3.0293|0.2205|0.1457|
|**Income and productive activi**|**ties**||||
|Num. productive ha of land|1.7492|1.7708|0.0215|0.9048|
|log (HH monthly income PC)|4.8815|4.8130|-0.0685|0.1003|
|**HH. Characteristics and asse**|**ts**||||
|Dirt foor*|0.7271|0.6945|-0.0326|0.2831|
|Electricity*|0.6679|0.6572|-0.0106|0.8239|
|Refrigerator*|0.0463|0.0452|-0.0011|0.9262|
|Television*|0.3751|0.3359|-0.0392|0.2528|
|Draft animals*|0.3518|0.3818|0.0301|0.3222|
|**Household demographics**|||||
|Household size|6.8539|6.8566|0.0027|0.9770|
|Num children 0-7|2.1263|2.0936|-0.0327|0.5062|
|Num children 8-17|2.1323|2.1558|0.0235|0.6716|
|Num adults_>_70|0.0692|0.0706|0.0015|0.8689|
|**Localities characteristics**|||||
|Marginalization index 1995|0.6748|0.5296|-0.1452|0.1352|
|Num. observations|1,663|2,831|||

* Dummy variable

This table tests balance in observable characteristics between the PROSPERA RCT original treatment and control with our sample. Observations are restricted to those households that were found in ENCEL 2017-18 and employed in our main estimations. Balance of variables shown are calculated with the 1997 ENCASEH data. Standard errors clustered at the locality level. Asterisks indicate significance at the ***1%, **5%, and *10% level.

11
geographical coverage, individuals were not found in the address given to surveyors or they did not respond. In addition, a sub-sample of 1,994 individuals outside the relevant age groups was mistakenly surveyed.<sup>10</sup> In our analysis we use all the individuals sampled.

Table 3 gives further detail about the different possibilities of sample attrition. In this table we use a logit model to relate household baseline characteristics with the probability of attrition. Even columns add the interaction of the baseline characteristics with the treatment dummy to further explore the possibility of selective attrition. In columns (1) to (4) we present evidence about the attrition of the original households, which are the foundation of the sampling design. Columns (1) and (2) give evidence of the locality selection (similarly as in Table 1 Panel A) while columns (3) and (4) give evidence of the possibility to find respondents in the selected 334 localities. As these columns show, older head members of smaller households are more likely to be missing. This is consistent with the evidence presented in Table 1, where we found no evidence of selective attrition. Finally, columns (5) and (6) include newly formed household attrition. Given that these households did not exist in 1997, its attrition is based on the possibility to find members in the relevant ages that moved out of the original household. In this sense, the attrition results from the 4,207 members who were searched for and not found. Section VI.A.3 does a robustness exercise where inverse probability weights are employed to adjust for attrition.

**Available information.** Both for _original_ and _new_ households, dwelling’s characteristics and information on durable assets were gathered at the household level, we use such information to explore PROSPERA’s long-term impacts on welfare. Individuals in the critical age groups described were asked several additional questions on income and work-related topics. An important limitation of the ENCEL 2017 data is that non-durable consumption (crucially including food consumption) is not available. This somewhat constrains our welfare analysis, especially for a poor population context, where food expenditure represents a high proportion of total expenditures. However, as an additional exercise, we propose an imputed measure on non-durable consumption expenditure, which includes food, personal products, and clothing, adapting the methodology of Blundell et al. (2005) and Attanasio and Pistaferri (2016) to the available data and context (see Appendix Section C). It is important to remind the reader that while durable consumption items are typically bigger ticket items, their purchase is infrequent, and for poor households the total expenditure on durables is typically about 20% of total expenditure, so that providing evidence on non-durable expenditure seems rather important.

_Table 4_ gives descriptive statistics for the original and new households employed in our analysis using 1997 and 2017 data. For new households, the 1997 information corresponds to that of their respective household of origin. The comparison between 1997 and 2017 shows an

> 10These individuals added _by mistake_ are not a random sub-sample of all the individuals out of the group of interest, but correspond to those for whom age was not available in 1997-2000 and were mistaken for newborns.

12
<u>Table 3: Attrition table.</u>

|||Original H|ouseholds||New Ho|useholds|
|---|---|---|---|---|---|---|
||1997 dis|tribution|2017 dis|tribution|2017 dis|tribution|
||(1)|(2)|(3)|(4)|(5)|(6)|
|Loc. marg index|0.099|-0.052|-0.001|0.053|-0.021|0.155|
|<br>|(0.071)|(0.126)|(0.076)|(0.141)|(0.061)|(0.123)|
|Female head<sup>_†_</sup>|0.033|0.017|0.083|0.030|0.179|0.521***|
||(0.085)|(0.144)|(0.092)|(0.164)|(0.112)|(0.192)|
|Head’s age|0.020***|0.023***|0.022***|0.025***|0.008***|0.015***|
||(0.002)|(0.003)|(0.002)|(0.003)|(0.003)|(0.004)|
|Head’s yrs of school|-0.006|0.007|-0.005|0.005|0.002|0.001|
||(0.011)|(0.017)|(0.010)|(0.016)|(0.012)|(0.021)|
|Head indigenous<sup>_†_</sup>|-0.085|0.041|0.206**|0.120|0.125|-0.206|
||(0.087)|(0.158)|(0.086)|(0.157)|(0.084)|(0.169)|
|Household size|-0.31***|-0.31***|-0.37***|-0.37***|-0.02|-0.01|
||(0.016)|(0.027)|(0.020)|(0.035)|(0.017)|(0.026)|
|Assets PCA|-0.044*|-0.054|-0.011|0.020|0.015|-0.001|
||(0.024)|(0.042)|(0.022)|(0.039)|(0.022)|(0.038)|
|Dirt foor<sup>_†_</sup>|0.061|0.078|0.035|0.184|0.092|0.012|
||(0.070)|(0.126)|(0.068)|(0.118)|(0.070)|(0.120)|
|Owns Productive land<sup>_†_</sup>|0.032|-0.121|0.013|-0.165|0.109|0.011|
||(0.064)|(0.110)|(0.057)|(0.104)|(0.069)|(0.125)|
|Num children 8-17|0.056***|0.084***|0.068***|0.100***|0.042*|0.039|
||(0.019)|(0.030)|(0.022)|(0.036)|(0.024)|(0.038)|
|Treatment<sup>_†_</sup>|0.005<br>|0.138<br>|-0.032<br>|0.422<br>|0.021<br>|0.348<br>|
||(0.098)|(0.284)|(0.089)|(0.298)|(0.080)|(0.340)|
|T x Loc. marg index||0.236||-0.078||-0.245*|
|||(0.156)||(0.164)||(0.141)|
|T x Female head||0.017||0.084||-0.534**|
|||(0.179)||(0.198)||(0.234)|
|T x Head’s age||-0.005||-0.006||-0.010*|
|||(0.004)||(0.004)||(0.006)|
|T x Head’s yrs of school||-0.020||-0.016||-0.000|
|||(0.022)||(0.021)||(0.025)|
|T x Head indigenous||-0.180||0.122||0.468**|
|||(0.192)||(0.186)||(0.192)|
|T x Household size||-0.001||-0.013||-0.012|
|||(0.034)||(0.042)||(0.034)|
|T x Assets PCA||0.015||-0.050||0.019|
|||(0.052)||(0.047)||(0.046)|
|T x Dirt foor||-0.025||-0.221||0.116|
|||(0.152)||(0.143)||(0.147)|
|T x Owns productive land||0.250*||0.281**||0.144|
|||(0.134)||(0.123)||(0.149)|
|T x Num children 8-17||-0.042||-0.051||0.011|
|||(0.039)||(0.045)||(0.048)|
|Constant|1.408***|1.329***|1.268***|0.976***|-0.101|-0.286|
||(0.150)|(0.223)|(0.139)|(0.240)|(0.173)|(0.270)|
|T x interactions (p-value)||0.678||0.331||0.075|
|Observations|12,163|12,163|9,635|9,635|6,905|6,905|
|Mean|0.641|0.641|0.541|0.541|0.607|0.607|

This table shows the relationship between attrition, based on the capability to find the original households from the 1997 ENCASEH sample, and household and locality characteristics measured at baseline with 1997 ENCASEH data (columns 1 to 4). Columns 3 and 4 only include households in localities sampled in 2017 ENCEL. In columns 5 and 6 attrition is defined based on the capability to find young members who formed their own household. Standard errors clustered at the locality level.<sup>_†_</sup> indicates a dummy variable. Asterisks indicate significance at the ***1%, **5%, and *10% level.

13
increase in levels of education, greater income levels, more asset accumulation; original households aged and became more adult-based; new households are younger in general (both in terms of head age and members composition). Interestingly the proportion of female heads importantly increases.<sup>11</sup> Several reasons explain this change: females are the transfer recipients, this means that single-parent households would tend to be female, but also that when asked for the head 20-years after the program the likelihood of appointing the female (at least to the surveyor) is greater; overtime, female widows are more likely than male widowers; and finally upon households split it is more likely for the female to keep the children and the resources of the program.

Table 4: Descriptive Statistics.

||Original HH|New HH|
|---|---|---|
||1997<br>2017|1997<br>2017|
|**Household head characteristics**|||
|Female*|0.06<br>0.26|0.06<br>0.13|
|Age|40.33<br>56.82|41.00<br>31.25|
|Years of schooling|2.95<br>3.33|2.88<br>7.76|
|**Income**|||
|log(HH monthlyincome PC)|4.84<br>7.35|4.85<br>7.14|
|**HH characteristics and assets**|||
|Dirt foor*|0.71<br>0.14|0.69<br>0.13|
|Electricity*|0.66<br>0.98|0.66<br>0.97|
|Refrigerator*|0.05<br>0.66|0.04<br>0.56|
|Television*|0.35<br>0.83|0.36<br>0.82|
|**HH demographics**|||
|Household size|6.86<br>2.47|7.34<br>3.84|
|Num children 0-7 yrs|2.11<br>0|2.26<br>1.08|
|Num children 8-17 yrs|2.15<br>0|2.38<br>0.66|
|Num children 18-34 yrs|1.35<br>0.73|1.46<br>1.62|
|Num children 35-54 yrs|0.967<br>0.86|1.01<br>0.39|
|Num children 55-69 yrs|0.194<br>0.67|0.20<br>0.04|
|Num adults 70+yrs|0.070<br>0.17|0.07<br>0.02|
|**Localities characteristics**|||
|Marginalityindex(1995)|0.58|0.58|
|Observations|4,494|2,265|

* Dummy variables

This table shows descriptive statistics of household and individual level variables that we will use to build our main dependent variables, as well as controls that we will use in our main specifications. Data comes from: (i) 1997 ENCASEH, which corresponds to the baseline data for the Progresa experiment and (ii) 2017-18 ENCEL, which is the latest round of the experiment’s panel.

11It is important to indicate that these proportions of female headship are among eligible households.

14
## **IV.B INEGI’s 2015 Intercensus**

A second part of the analysis that will be detailed in the next section uses the 2015 intercensal survey, which is collected by INEGI.<sup>12</sup> This survey is gathered at the midpoint between censuses and contains information on individual’s income, education, dwelling’s characteristics, durable asset ownership, and consumption vulnerability measures (among other things). The survey includes information from individuals in more than 6 million households from all Mexican municipalities. The access to this data with restricted geographical identifiers was obtained through INEGI’s microdata lab.<sup>13</sup> Our analysis focuses on individuals aged 0 to 21 in 19972000 as those individuals had the highest potential exposure to PROSPERA. In total, we use 1,875,039 individuals in all the localities (urban and rural) from 24 Mexican states in our analysis.<sup>14</sup> Importantly, the use of this ulterior data source allows to look directly into measures of food consumption insecurity and resilience, while also allowing for a sharper definition of treatment status as we will explain later. At the same time with this much larger sample, we are also able to validate the results obtained from the previous data sources, in a fully representative sample of the Mexican population.<sup>15</sup>

# **V Empirical Strategy**

## **V.A Analysis Using the PROSPERA ENCEL Panel**

**Long-Term Effects.** For identification of the long-term effects of PROSPERA, we first rely on the 1997-2000 RCT experiment, which gives the cleanest source of variation available. However, since the control localities became treated about two years after the start of Progresa (i.e. by the end of 1999), this strategy should be interpreted as an _early_ versus _late treatment_ or as a treatment intensity deriving from the extra months of transfers the original treated received. _Table 5_ convincingly shows that original households in early treatment localities receive 8 _._ 8% larger transfers, during 6 _._ 6 additional two-month installments. However, these additional resources are not evenly distributed during the 20 year period between the start of the program and 2017, rather they are concentrated in 1998-99.

> 12Available at https://goo.gl/5EMD7e

> 13For confidentiality reasons, INEGI does not disclose the geographical identifiers for localities with fewer than 15,000 inhabitants. The researchers filled up a request to gain access to this information which is critical for the

> 14The selection of Mexican states for the analysis was based on the fact that a discontinuous jump was visually identified in the selection of localities. The states left out include Aguascalientes, Baja California, Colima, Chihuahua, Mexico City, Morelos, Nayarit, and Yucatan.

> 15Even though the exclusion of Mexico City might strike as harmful for the representativeness of the sample, it is important to remember that the urban extension of the program did not occur until 2004. At that time little variation of inclusion was left geographically, which is our main identification strategy here.

15
<u>Table 5: Total Cash Transfers.</u>

||(1)|(2)|(3)|
|---|---|---|---|
||log(Tot Transfers)|log(Pot Transfers)|Tot Payments|
|**_Panel A: Original Households_**||||
|Treatment|0.088**|0.062***|6.60***|
||(0.0358)|(0.0053)|(0.971)|
|Constant|11.17***|11.37***|92.11***|
||(0.0958)|(0.0170)|(2.728)|
|Observations|4,494|4,494|4,494|
|R-squared|0.105|0.794|0.039|
|Mean T 2017|12.29|12.66|106.92|
|Mean C 2017|12.20|12.60|100.59|
|**_Panel B: New Households_**||||
|Treatment|0.091**|0.055***|5.83***|
||(0.0449)|(0.00730)|(1.198)|
|Constant|11.34***|11.42***|100.20***|
||(0.131)|(0.0250)|(3.606)|
|Observations|2,265|2,265|2,265|
|R-squared|0.118|0.807|0.037|
|Mean T 2017|12.36|12.71|107.65|
|Mean C 2017|12.28|12.67|102.03|

This table shows the direct implications of the randomized treatment variable in terms of the cash transfers received at the beginning of the program (1998-99). The outcomes employed are: (i) _Total transfers_ , which correspond to the accumulated amount of transfers received by the households (in real Mexican pesos); (ii) _Potential transfers_ , which refers to the amount of transfers that, given the program rules, a household would accumulate if there is perfect compliance; and (iii) _Total Payments_ , which indicates the total amount of installments that a household received since they were enrolled into the program. This information comes from administrative records from the program. Treatment is a dummy variable that identifies if the observation belongs to one of the 320 original Progresa RCT treatment localities. Controls include (from ENCASEH 1997): HH head age, education, speaking a dialect, HH size, % members under 15, dummies for home, productive land and draft animals ownership, and locality marginalization index. Standard errors clustered at the locality level. Asterisks indicate significance at the ***1%, **5%, and *10% level.

As we use the initial RCT design for the analysis, the estimation of the effects of interest is rather simple and consists of the following specifications: where _Tj_ is a dummy identifying those households living in an early treatment locality _j_ (randomly determined), _Xij_ is a set of controls at the household ( _i_ ) and locality level ( _j_ ).<sup>16</sup> As standard in the literature we presents results on the three specifications above to provide evidence on the robustness of the results. In equation (1) we employ a simple cross-sectional difference approach, where the parameter of interest is _τ_ 1 in particular this approach is useful 16Even though we have a smaller sample than the 506 original localities, as explained in further detail in section IV, we made sure that attrition across localities is not differential by treatment status and redid a balance test using our available sample. _Table 2_ in the appendix shows that treatment and control households are still balanced.

16
as certain outcomes (specific durable categories IT items and services) are not collected at baseline. However, even if specific outcomes are not recorded at baseline we could still implement both other approaches by replacing the baseline missing information with durable items that are correlated with the missing ones (e.g. the full set of durables). In equation (2) we use a standard difference-in-differences approach, where the parameter of interest is _α_ 3 describing the excess variation in the outcomes between treated and controls with **1** _{_ 2017 _t}_ an indicator dummy for the 2017 wave. Equation (3) is commonly referred to as an ANCOVA specification which allows for some extra flexibility with respect to the DiD and is more appropriate from an inferential viewpoint. In the latter specification the parameter of interest is _β_ 1, while _Yij_ (1997) indicates the outcome value at baseline (1997) (see McKenzie 2012).

**Lifecycle and Intergenerational Effects.** For the analysis of the lifecycle and intergenerational effects of PROSPERA, we employ a modification of equation 3, as is standard in this literature, by relating baseline outcomes (for the original household when appropriate) to current ENCEL 2017-18 outcomes. We explore the effects on mobility over generations and across treatment status using:

where ∆ _Yij_ = _Y_ ( _G_ 2) _ij_ (2017) _− Y_ ( _G_ 1) _ij_ (1997) gives the change in the outcome through time for the children with respect to their parents. _Y_ ( _G_ 2) _ij_ (2017) is the outcome of the next generation or new households (denoted with _G_ 2) observed in 2017, while _Y_ ( _G_ 1) _ij_ (1997) is the outcome of their parents ( _G_ 1) observed at the time the program was about to start: the baseline (ENCASEH 1997). The coefficient _η_ 2, is essentially one-minus-the coefficient of intergenerational persistence as it indicates the stability of outcomes across generations. In this formulation we are also interested in both _η_ 1 and _η_ 3, as the first is the baseline effect of the policy with respect to control individuals or households while _η_ 1 + _η_ 3 is the corresponding parameter for the early treated. If we take equation (4) and replace _Y_ ( _G_ 2) _ij_ (2017) with _Y_ ( _G_ 1) _ij_ (2017) (parents’ outcome observed in 2017), _η_ 1 and _η_ 3 would give information about lifecycle effects for the treatment group. Following Chetty et al. (2014), in this analysis we employ as outcomes the relative position of the household using the percentile of three different measures: schooling, a durable asset index and income. Each percentile is calculated within groups formed by 10-year window age ranges.

# **V.B Analysis Using the Intercensus**

To avoid the small window provided by the early versus late treatment identification, we complement the previous analysis with a difference-in-difference (DiD) strategy that employs the program’s roll-out and different age groups. For this purpose, we create four groups of localities based on their enrollment year into PROSPERA: (i) E1, which indicates localities enrolling 17
in 1997-98; (ii) E2, corresponding to entering in 1999-2001; (iii) E3, which relates to localities entering in 2002-2005; and (iv) E4, which identifies those localities entering after 2006. Early versus late enrollment comparison implies receiving more transfers, but if paired with an individual’s age it might also give different incentives based on the schooling conditionality, further for those individuals whose age is above the threshold for receiving PROSPERA’s transfers at the time their locality enters the program this also means that they will never be directly treated.

As poorer localities were in general treated first, we need to deal with the selection bias. Following Duflo (2001) and Parker and Vogl (2018), we begin by taking care of the selection problem by using different cohorts, which proxy an individual’s exposure to the program when interacted with the roll-out. Four cohorts are formed using individuals’ ages in 2001:

- (C1) 0-5 years, which corresponds to individuals who had not begun primary school when their locality enrolled, but if enrolled in 1997-98 they possibly benefited in early stages of their development.

- (C2) 6-10 years, which corresponds to individuals more sensitive to their locality’s date of enrollment because of the program’s conditionalities. For instance, if enrolled in the early groups (before 2002) they would still be in primary school when their locality entered the program. However, if enrolled later (e.g. 2006) they are likely to be in secondary.

- (C3) 11-16 years, which corresponds to individuals in critical schooling stages: if enrolled early (before 2002) they are likely in late primary or early secondary school years, but if enrolled late they are likely past this stage. Also this age range has a high likelihood of being employed by 2017-2018.

- (C4) 17-22 years, which is taken as a control group since regardless of year of enrollment they are past critical stages of schooling in terms of the conditionalities, as such they will never be directly treated.

The specification for the DiD estimation is: where _Yij_ is the 2015 outcomes for individual _i_ of locality _j_ , _Cki_ are the cohorts defined above, and _Eqj_ are the localities’ groups based on their year of enrollment (as defined above). Our parameters of interest are the _τ_ ’s, which correspond to the DiD estimates. For instance, in our results we will compare _τk,_ 1, _τk,_ 2, and _τk,_ 3, which give the effects of different levels of program exposure for a given cohort ( _k_ ). In this case, keeping as reference cohort C4 means that these _τ_ ’s control for selection bias using the reference cohort C4, which is not benefited by the program regardless of the enrollment date.

18
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# **VI Results**

## **VI.A Original Experiment**

As described above, we begin by analyzing the effects of the early versus late treatment using the 1997 original experimental design that assigned 320 of 506 localities to receive government transfers as early as 1998 and all the way to the end of 1999. We estimate equations (1), (2), (3) and present the results in the corresponding panels A to C of _Tables 6 and 7_ . We look at durable assets, imputed non-durable (food, personal products, and clothing) expenditures, further to income and schooling, as outcomes of interest and to original and new households, respectively, as were defined in section IV. Our interest here is to analyze the durable expenditure behavior in line with the long-term perspective of the overall report and the original spirit of the program.

### **VI.A.1 Original Households**

_Table 6_ displays no significant differences for treated vs. control original households in most cases. The outcomes employed in the analysis are an aggregation (counting) of different durable goods, a different aggregation through prices for example would be problematic given the large variation in quality and vintage for durable goods. We therefore present a counting exercise on the following assets: (i) transportation, which refers to number of vehicles (cars, vans, motorcycles); (ii) entertainment, which includes TV, radio and sound equipment; (iii) kitchen supplies, which adds number of blenders, refrigerators, microwaves, gas stove or electric grills; (iv) basic housing services, which identifies having firms floor, electricity, drainage and water connection in the property; (v) IT assets, which refers to computers and cellphones; and (vi) IT and entertainment services, which include home phone, internet and pay-TV.<sup>17</sup> We note that as some of the IT and IT and Entertainment goods are not available in the baseline wave (1997) when we produce the analysis for such goods in the DiD and ANCOVA specifications we use as baseline measures the full aggregation of durables.

In Panel B of _Table 6_ we perform a testing strategy based on the excess growth of the durable goods in treated vs. control households; while in Panel C we present a standard ANCOVA specification, i.e. where we regress follow-up outcomes on treatment and control for baseline outcomes. The results suggest that in general there are no baseline differences, confirming that the initial randomization is still valid and that the random selection of households for the last follow-up or non-differential attrition rates for the most part, see the coefficients attached to the Treatment dummy. However, in some of the cases, the treatment dummy (outcome in 1997) displays significant, yet negative, differences. The differences resulting from the passing of time (2017 dummy) shows that access to the assets has greatly improved for all items, not surprisingly given that the two waves are 20 years apart, this signals a general improvement in

> 17A good-by-good analysis is also available upon request.

20
Table 6: Effects on durable good’s accumulation. Original households.

||(1)<br>Transport|(2)<br>Entert eq|(3)<br>Kitchen sup|(4)<br>Basic serv|(5)<br>IT items|(6)<br>IT serv|(7)<br>ln(impcons)|
|---|---|---|---|---|---|---|---|
|**_Panel A: Cross-sectio_**|**_n_**|||||||
|Treatment|-0.023|0.011|-0.054|-0.002|-0.019|0.020|-0.011|
||(0.023)|(0.044)|(0.050)|(0.048)|(0.027)|(0.036)|(0.011)|
|Constant|0.289***<br>(0.057)|1.380***<br>(0.099)|1.804***<br>(0.121)|2.709***<br>(0.088)|0.738***<br>(0.071)|0.236***<br>(0.075)|8.713***<br>(0.026)|
|Observations|4,494|4,494|4,494|4,494|4,494|4,494|4,182|
|**_Panel B: DiD 1997-2_**|**_017_**|||||||
|Treatment X 2017|0.006|0.098**|0.066|-0.068|0.082|0.127|0.014|
||(0.027)|(0.049)|(0.058)|(0.077)|(0.102)|(0.107)|(0.011)|
|Treatment|-0.017|-0.103**|-0.106**|0.034|-0.158**|-0.162**|-0.023**|
||(0.012)|(0.040)|(0.043)|(0.063)|(0.080)|(0.079)|(0.009)|
|2017|0.217***<br>(0.022)|0.444***<br>(0.038)|1.443***<br>(0.046)|1.279***<br>(0.061)|-0.801***<br>(0.078)|-1.077***<br>(0.081)|0.090***<br>(0.008)|
|Constant|0.030<br>(0.030)|0.786***<br>(0.079)|0.311***<br>(0.091)|1.361***<br>(0.085)|1.212***<br>(0.104)|1.099***<br>(0.105)|8.639***<br>(0.020)|
|Observations|8,988|8,988|8,988|8,988|8,988|8,988|8,656|
|**_Panel C: ANCOVA_**||||||||
|Treatment|-0.020|0.028|-0.029|-0.002|-0.011|0.026|-0.002|
||(0.022)|(0.042)|(0.047)|(0.046)|(0.027)|(0.036)|(0.010)|
|Y(97)|0.522***<br>(0.077)|0.146***<br>(0.017)|0.279***<br>(0.019)|0.158***<br>(0.018)|0.038***<br>(0.008)|0.029**<br>(0.011)|0.383***<br>(0.032)|
|Constant|0.295***|1.287***|1.731***|2.504***|0.704***|0.210***|5.401***|
||(0.057)|(0.098)|(0.116)|(0.088)|(0.071)|(0.075)|(0.279)|
|Observations|4,494|4,494|4,494|4,494|4,494|4,494|4,169|
|Mean T 2017|0.247|1.473|1.928|2.532|0.656|0.426|9.052|
|Mean C 2017|0.241|1.435|1.891|2.497|0.662|0.386|9.041|

This table shows the long-term effects of the program on a set of variables that result from aggregating groups of durable assets and household characteristics. Observations are restricted to households from 1997 that were successfully found again in 2017 (original households). The outcomes constructed are: (1) _Transportation_ , which adds the number of cars and vans; (2) _Entertainment equipment_ , which gathers under entertainment equipment number of TV, radio and sound equipment; (3) _Kitchen supplies_ , which sums the following appliances: blender, refrigerator, electric grill, gas stove or microwave oven; (4) _Basic services_ , which consists of the availability of the following services: firm floor, electricity, drainage and water access in the property; (5) _IT items_ , which refer to the number of computers and cellphones; and (6) _IT services_ , which sums the home phone, internet and pay-TV; (7) _ln(imp cons)_ , is the imputed measure of nondurable expenditure on food personal products, and clothing. Data employed comes from 1997 ENCASEH and 2017-18 ENCEL. Panel A shows the result from a cross-section estimate which only uses data from 2017. Treatment is a dummy variable that identifies if the observation belongs to one of the 320 original Progresa RCT treatment localities. Panel B does a DiD estimation with 1997 and 2017 as the two periods considered. Panel C estimates an ANCOVA, which controls for the pre-existing level of the dependent variable (denoted as Y(97)). Controls include (from ENCASEH 1997): HH head age, education, speaking a dialect, HH size, % members under 15, dummies for home, productive land and draft animals ownership, and locality marginalization index. Standard errors clustered at the locality level. Asterisks indicate significance at the ***1%, **5%, and *10% level.

21
the lives of the original households. Finally, we find a significant but small difference in the entertainment variable. On non-durable expenditure we find no effects.

Several possible explanations could justify these results. First, as already described, our treatment definition means having additional transfers in the first year of the program, which by now was 20 years ago. These additional resources might have had an effect in the short and medium term, as several papers and reports have shown. However, such effect might not have carried through 2017. Second, we are looking at households that also existed in 1997, which means that they are predominately composed of older members and increasingly headed by females. Being mostly focused towards benefiting the next generations, PROSPERA might yield lower impacts in this older-aged group. Third, the sample might not be large enough to enable researchers to detect statistically significant differences. Fourth, we are using durable assets that in the past have been used to identify eligible (poor) households. This might motivate respondents not to respond truthfully if they believe that the survey could be used as part of the assignment process.<sup>18</sup> Fifth, it is notoriously complex to look at durables expenditures as these are infrequent purchases of wide quality variation, the data available so far do not include the prices of such purchases; further the available data at this stage do not include non-durable or food consumption directly, so that we resort to an imputation method which has clear advantages but also a number of disadvantages as any imputation. The imputation procedure is described, as mentioned, in Appendix C. Sixth, the original households might have passed on to their offspring some of their assets or savings and therefore we might not see a positive difference with the control households. One should bear in mind that PROSPERA by design targets children and therefore it is plausible that the main long-run positive effects are found among those who were the primary target of the policy in terms of health, nutrition, and schooling. While the original households might have had an initial bump in their incomes, that was fairly limited in the original experiment, so that eventually the original control household might have caught up. The same does not need to be true for the treated children as some of the control children, given their age and school grades, might not be affected at all by the late roll out of the program in control localities. For example, those children at the margin of dropping out of school who were in the control villages would have dropped our while their counterparts in treatment villages would have stayed in school.

# **VI.A.2 New Households**

In this section we analyze the effects for durable goods purchase, and imputed consumption expenditures, by the new households as previously defined: these are mostly the offspring of the original households, potentially those children in 1997 that were the target of the policy. As these new households are composed by the direct beneficiaries of the program transfers, they 18With certain regularity PROSPERA gathers a similar survey called ENCASEH, whose purpose is to determine if the households are still in poverty and should stay in the program or not.

22
are perhaps the most interesting group to look at. Importantly, as we describe in _Table 4_ the new households are younger (as expected), on average the head of household is 31 years old, and, on average, has about 5 more years of education than their parental households. Further the household size is smaller than that of the original households in 1997 with a size of about 4 members compared to 7 members for their parental household. These are in practice young households with fewer, more educated members. We also note that being an early entrant in PROSPERA is not predictive of receiving PROSPERA transfers in 2017, i.e. both offspring of early and late treated households are equally likely to receive PROSPERA in 2017. In _Table 7_ we present the results for these new households. An important motivation for conducting a separate analysis for these households, comes from the fact that the program has as one of its main purposes breaking the cycle of poverty transmitted from parents to sons and daughters. New households will be mostly composed of members that were children in 1997. For these households, the results are more encouraging: in the case of entertainment equipment, kitchen supplies and IT and entertainment services, the effects are positive and significant. Also, the size of the effect is non-negligible, it represents an increase in durable goods of between 7% and 16% of the “control” households. Further, on imputed consumption the effects are positive and significant at about a 5% increase in non-durable expenditure, a non-trivial effect considering the margin of treatment used here.

Given that we are looking into new households, i.e. households composed by individuals who have moved out of their original households, we need to consider that the household formation process might not be purely random. For this reason, in _Table 8_ we provide evidence on the strength of such selection mechanism, and we show that the program does not produce strong evidence of motivating young individuals moving out of the parental household on average (column 1 _Table 8_ ). In both, treatment and control, the proportion of individuals moving out from home and creating their own new household is 60%. However this average effect masks a more nuanced behavior when looking at different age groups as we do in column 2, it turns out that very young children (0-5 years old in 1997) tend to remain with the original household longer, while the older children (11-16 years old in 1997) move out earlier to form their own household. Similarly, and importantly for the program, these same older children are more likely to migrate outside the locality of birth, in fact given the magnitude of the coefficients on new household formation and migration it seems that a large fraction of the new households are formed in different locations than those of the parents. The migration behavior is once more consistent with the human capital accumulation channel, migration being part of it or simply a way to reap the benefits of higher human capital. For these reasons, we test whether those who migrated chose a large city (Mexico City, Guadalajara, or Monterrey) as typically larger cities provide more opportunities for growth (Moretti 2012; De La Roca and Puga 2017). While this latter test is tentative in nature as it relies upon a selected sample of migrants, it would have provided some interesting thoughts, however it appears that there is no 23
specific large correlation between being treated and moving to a big city for any of the groups. We note that the results for the new households are robust to controlling for the new household being itself a PROSPERA recipient.

Table 7: Effects on durable good’s accumulation. New households.

||(1)<br>Transport|(2)<br>Entert eq|(3)<br>Kitchen sup|(4)<br>Basic serv|(5)<br>IT items|(6)<br>IT serv|(7)<br>ln(impcons)|
|---|---|---|---|---|---|---|---|
|**_Panel A: Cross-sectio_**|**_n_**|||||||
|Treatment|-0.001|0.092**|0.158**|0.067|0.035|0.059*|0.036**|
||(0.024)|(0.045)|(0.062)|(0.042)|(0.034)|(0.035)|(0.014)|
|Constant|0.223***|1.529***|1.847***|2.456***|0.779***|0.337***|8.826***|
||(0.080)|(0.153)|(0.170)|(0.109)|(0.093)|(0.114)|(0.037)|
|Observations|2,265|2,265|2,265|2,265|2,265|2,265|2,152|
|**_Panel B: DiD 1997-2_**|**_017_**|||||||
|Treatment X 2017|0.014|0.194***|0.244***|0.025|0.197*|0.217*|0.054***|
||(0.028)|(0.067)|(0.070)|(0.087)|(0.118)|(0.125)|(0.014)|
|Treatment|-0.011<br>(0.014)|-0.115**<br>(0.052)|-0.080<br>(0.052)|0.032<br>(0.069)|-0.186*<br>(0.102)|-0.184*<br>(0.102)|-0.017<br>(0.011)|
|2017|0.170***|0.312***|1.338***|1.232***|-0.735***|-1.166***|0.208***|
||(0.023)|(0.051)|(0.052)|(0.063)|(0.090)|(0.099)|(0.009)|
|Constant|0.016|1.013***|0.422***|1.345***|1.318***|1.313***|8.644***|
||(0.043)|(0.125)|(0.123)|(0.104)|(0.143)|(0.146)|(0.027)|
|Observations|4,530|4,530|4,530|4,530|4,530|4,530|4,407|
|**_Panel C: ANCOVA_**||||||||
|Treatment|0.001|0.096**|0.173***|0.066|0.045|0.060*|0.042***|
||(0.024)|(0.045)|(0.060)|(0.041)|(0.034)|(0.035)|(0.013)|
|Y(97)|0.195**<br>(0.081)|0.035<br>(0.027)|0.209***<br>(0.034)|0.039**<br>(0.018)|0.047***<br>(0.010)|0.006<br>(0.014)|0.310***<br>(0.045)|
|Constant|0.227***|1.501***|1.776***|2.399***|0.726***|0.330***|6.139***|
||(0.080)|(0.155)|(0.168)|(0.111)|(0.095)|(0.117)|(0.398)|
|Observations|2,265|2,265|2,265|2,265|2,265|2,265|2,149|
|Mean T 2017|0.208|1.450|1.992|2.605|0.840|0.428|9.241|
|Mean C 2017|0.200|1.354|1.793|2.522|0.793|0.361|9.203|

This table shows the long-term effects of the program on a set of variables that result from aggregating groups of durable assets and household characteristics. Observations are restricted to newly formed households in 2017 (new households) that were identified by searching for members no longer present in their original 1997 households. The outcomes constructed are: (1) _Transportation_ , which adds the number of cars and vans; (2) _Entertainment equipment_ , which gathers under entertainment equipment number of TV, radio and sound equipment; (3) _Kitchen supplies_ , which sums the following appliances: blender, refrigerator, electric grill, gas stove or microwave oven; (4) _Basic services_ , which consists of the availability of the following services: firm floor, electricity, drainage and water access in the property; (5) _IT items_ , which refer to the number of computers and cellphones; and (6) _IT services_ , which sums the home phone, internet and pay-TV; (7) _ln(imp cons)_ , is the imputed measure of non-durable expenditure on food personal products, and clothing. Data employed comes from 1997 ENCASEH and 2017-18 ENCEL. Panel A shows the result from a cross-section estimate which only uses data from 2017. Treatment is a dummy variable that identifies if the observation belongs to one of the 320 original Progresa RCT treatment localities. Panel B does a DiD estimation with 1997 and 2017 as the two periods considered. Panel C estimates an ANCOVA, which controls for the pre-existing level of the dependent variable (denoted as Y(97)). Controls include (from ENCASEH 1997): HH head age, education, speaking a dialect, HH size, % members under 15, dummies for home, productive land and draft animals ownership, and locality marginalization index. Standard errors clustered at the locality level. Asterisks indicate significance at the ***1%, **5%, and *10% level.

24
Table 8: New household formation and migration.

||(1)<br>New HH|(2)<br>New HH|(3)<br>Migrated|(4)<br>Migrated|(5)<br>Metropolis|(6)<br>Metropolis|
|---|---|---|---|---|---|---|
|Treatment|-0.009|0.015|0.022|-0.033|0.005|-0.004|
||(0.0216)|(0.0415)|(0.0234)|(0.0398)|(0.0308)|(0.0577)|
|T x (0-5)||-0.122***||0.026||0.030|
|||(0.0403)||(0.0358)||(0.0543)|
|T x (6-10)||0.062||0.095**||0.004|
|||(0.0443)||(0.0402)||(0.0572)|
|T x (11-16)||0.117**||0.114***||-0.031|
|||(0.0454)||(0.0418)||(0.0600)|
|Constant|0.351***|0.379***|-0.001|0.019|-0.061|-0.060|
||(0.0642)|(0.0657)|(0.0608)|(0.0619)|(0.105)|(0.106)|
|Observations|3,351|3,351|3,351|3,351|969|969|
|R-squared|0.017|0.041|0.011|0.016|0.044|0.046|
|Mean C|0.573||0.273||0.127||
|Mean C (0-5)||0.261||0.261||0.133|
|Mean C 6-10||0.603||0.272||0.104|
|Mean C 11-16||0.788||0.370||0.176|
|Mean C 16+||0.731||0.172||0.000|

This table consists of LPMs where the purpose is to identify if the treatment might have induced new household formation or migration out of the original household. The unit of observation are individuals in relevant age groups, as described in section IV. The outcomes are dummies that correspond to: (i) _New Household_ , which identifies if the individual inhabits in a new household (as opposed to an original household); (ii) _Migrated_ , which identifies if the individual migrated to a different locality from which the original household was located; and (iii) _Metropolis_ indicates if such migration had as destination either Mexico City, Guadalajara or Monterrey, which are the main urban Mexican cities. Controls include (from ENCASEH 1997): HH head age, education, speaking a dialect, HH size, % members under 15, dummies for home, productive land and draft animals ownership, and locality marginalization index. Standard errors clustered at the locality level. Asterisks indicate significance at the ***1%, **5%, and *10% level.

25
# **VI.A.3 Re-weighted Estimates**

_Table 9_ shows the results from re-weighting the observations in the sample in order to replicate the results that would have been obtained without attrition. Given that attrition occurred in different forms, we produce three different comparisons. The method employed for the reweighting is the inverse probability weighting (DiNardo et al., 1996). As a first step, a logit model of attrition with respect to a group of variables is estimated. All the observations are employed at this stage since baseline explanatory variables from the 1997 ENCASEH are used to predict attrition. Based on the results of this logit, a weighting factor is calculated to be used with the analysis sample from the previous estimations.

Table 9: Re-weighted estimates of long-term effects on durable good’s accumulation.

||(1)<br>Transport|(2)<br>Entert eq|(3)<br>Kitchen sup|(4)<br>Basic serv|(5)<br>IT items|(6)<br>IT serv|(7)<br>ln(impcons)|
|---|---|---|---|---|---|---|---|
|**_Panel A: Original Ho_**|**_useholds_**|||||||
|_1. Analysis Sample_||||||||
|Treatment|-0.020|0.028|-0.029|-0.002|-0.011|0.026|-0.002|
||(0.022)|(0.042)|(0.047)|(0.046)|(0.027)|(0.036)|(0.010)|
|Observations|4,494|4,494|4,494|4,494|4,494|4,494|4,169|
|_2. Original Distributi_|_on_|||||||
|Treatment|-0.016|-0.002|-0.025|-0.004|-0.011|0.029|-0.005|
||(0.021)|(0.043)|(0.047)|(0.049)|(0.028)|(0.033)|(0.010)|
|Observations|4,471|4,471|4,471|4,471|4,471|4,471|4,150|
|_3. Localities 2017 dis_|_tribution_|||||||
|Treatment|-0.016|-0.001|-0.027|-0.004|-0.014|0.033|-0.005|
||(0.021)|(0.043)|(0.047)|(0.048)|(0.028)|(0.033)|(0.010)|
|Observations|4,471|4,471|4,471|4,471|4,471|4,471|4,150|
|Mean T 2017|0.247|1.473|1.928|2.532|0.656|0.426|9.052|
|Mean C 2017|0.241|1.435|1.891|2.497|0.662|0.386|9.041|
|**_Panel B: New House_**|**_holds_**|||||||
|_1. Analysis Sample_||||||||
|Treatment|0.001|0.096**|0.173***|0.066|0.045|0.060*|0.042***|
||(0.024)|(0.045)|(0.060)|(0.041)|(0.034)|(0.035)|(0.013)|
|Observations|2,265|2,265|2,265|2,265|2,265|2,265|2,149|
|_2. Localities 2017 dis_|_tribution_|||||||
|Treatment|-0.005|0.076|0.144**|0.052|0.041|0.054|0.040***|
||(0.026)|(0.049)|(0.065)|(0.043)|(0.036)|(0.037)|(0.013)|
|Observations|1,912|1,912|1,912|1,912|1,912|1,912|1,822|
|Mean T 2017|0.208|1.450|1.992|2.605|0.840|0.428|9.241|
|Mean C 2017|0.200|1.354|1.793|2.522|0.793|0.361|9.203|

This table shows the long-term effects of the program on a set of variables that result from aggregating groups of durable assets and household characteristics. The reweighting strategy employed is the inverse probability weight (DiNardo et al., 1996). In Panel A observations are restricted to households included in 1997 ENCASEH (original households), while in Panel B observations are restricted to newly formed households in 2017 (new households) that were identified by searching for members no longer present in their original 1997 households. The reweighting strategy seeks to reproduce the original sample distribution. Two different target distributions are set following the attrition analysis done in _Table 3_ . _Original Distribution_ means the 1997 sample, which corresponds to the original households in the 506 localities. The purpose is to make our results comparable to the vast literature that focuses on this group. _Localities 2017 distribution_ is based on the 334 localities chosen for the sample and assumes that all the original 1997 households in those localities would have been found. The outcomes employed are: (1) _Transportation_ , which adds the number of cars and vans; (2) _Entertainment equipment_ , which gathers under entertainment equipment number of TV, radio and sound equipment; (3) _Kitchen supplies_ , which sums the following appliances: blender, refrigerator, electric grill, gas stove or microwave oven; (4) _Basic services_ , which consists of the availability of the following services: firm floor, electricity, drainage and water access in the property; (5) _IT items_ , which refer to the number of computers and cellphones; and (6) _IT services_ , which sums the home phone, internet and pay-TV; (7) _ln(imp cons)_ , is the imputed measure of non-durable expenditure on food personal products, and clothing. Data employed comes from 1997 ENCASEH and 2017-18 ENCEL. The table shows the results from an ANCOVA estimate, which controls for the pre-existing level of the dependent variable (denoted as Y(97)). Controls include (from ENCASEH 1997): HH head age, education, speaking a dialect, HH size, % members under 15, dummies for home, productive land and draft animals ownership, and locality marginalization index. Standard errors clustered at the locality level. Asterisks indicate significance at the ***1%, **5%, and *10% level.

26
Panel A refers to original households. Two sources of attrition are considered, as described in section IV.A: (i) localities composition, which means that just a sub-sample of the 506 original localities was surveyed; and (ii) response attrition, which means that some households in the selected localities were not found. In the first part of Panel A (Analysis sample) we show the main results estimated with the ANCOVA for original households for comparative reasons. Next, we show the results if no attrition happened (Original distribution). This results correspond to the household distribution in 506 and we add it for comparative reasons with respect to the original literature about the program. The reweighting factor employed for this result is the one included in column (1) of _Table 3_ . As can be seen, no significant effects on asset accumulation are obtained for this reweighted sample. Afterwards, in the third part of Panel A, we show the results that would be obtained if we only control for the response attrition. That is, the purpose is to replicate the distribution of all the households in the selected 334 localities. The reweighting factor in this case corresponds to column (3) of _Table 3_ . Again, no significant effects in asset accumulation are found. These results were expected since the attrition analysis suggested that no differential attrition between treatment groups was found.

Panel B refers to the new households. For this group attrition seems to be more relevant. Attrition here refers to the impossibility of finding all the individuals in the relevant age groups that exited their households to form a new one (or joined another household). Columns (5) and (6) in _Table 3_ show the attrition analysis for this group. To start with, a small proportion of individuals was found (40%). Second, the attrition analysis shows some slight significant differences between treatment and control (the joint test with the interaction terms has a p- value of 0.075). For this reason, we perform the reweighting strategy using the results from column (6) where the interaction terms were included. This reweighting factor would replicate the household distribution that would result if all the individuals in the relevant age groups that moved out of their original household were found in their new household. The results are shown in comparison to the main ANCOVA results (Analysis sample). As can be seen in the table, the results in asset accumulation are very similar to the resulting analysis with the sample found.

# **VI.B Youths and Intergenerational Transmission**

It is paramount when looking at long-term effects of such an important program to look at the life-cycle as well as at the intergenerational effects, ultimately the long-term success of the policy will be based on the success of the offspring of the originally treated households or the children who directly benefited from the government transfers as well as the other components of the program.

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# **VI.B.1 Effects in the Relevant Age Group**

To better explore the effects on the sample of individuals that form the “next generation”, we take the individuals classified in the group of interest, given their age. Recall, that this includes individuals who in 1997 were newborn, just beginning school or at sixth grade. For example, if we look at the effects of PROSPERA for those who benefit from the policy over their life, we are looking at the effect of exposure to the policy on their lifecycle outcomes. Relatedly, we could be interested in understanding whether the offspring of original households who are themselves beneficiaries of the transfers are faring better than their parents. This latter would be looking at intergenerational mobility and transmission of income, human capital, and consumption. Both dimensions are rather important as the lifecycle view will investigate whether being treated at an earlier stage of life could have long-lasting consequences (as in Hoddinott et al. 2008 and Martorell 2017); in the intergenerational view that is addressing the link between parents and offspring and how PROSPERA can foster upward mobility in society by improving the lives of the next generation with respect to those of their parents.

_Table 10_ suggests that it is this group of individuals driving the positive results for the new households, since entertainment equipment, kitchen supplies, and non-durable expenditure display significant effects in this analysis with similar magnitudes to those previously found. Panel B explores the heterogeneity of the effects distinguishing between young members still living in the original household and those that formed their household. This analysis confirms our previous hypothesis: it is the case that the young members that formed their own households significantly benefit from the program. Panel C also indicates that age-wise, the individuals driving the positive results correspond to those who were 11 to 16 in 1997 (i.e. those in their critical stages of schooling, where dropout rates were more common).

Importantly, this latter analysis confirms that those children at risk of dropping out of secondary schooling were in fact retained because of the program, those are the individuals aged 11-16 in 1997, and we find sustained positive effects in durable purchases and all other outcomes exactly for this group. However, we should stress that there is also redistribution of resources within the household as also older children in 1997 those older than 16, who for the large part were excluded from the direct schooling transfers as too old, seem to have benefited with respect to their control counterpart, certainly in terms of kitchen durables but also (albeit not significant) in the other durable categories. Here we note that, as evidence of the direct channel through improved human capital, the schooling results and partly the effect on income (not significantly different from zero) build a direct connection between the policy and its long-term effects. In Panel D, we investigate whether PROSPERA provided some insurance against health shocks of the head of household, we find that the positive effects of PROSPERA on durables and non-durables are somewhat also present for those households who suffered a health shock (albeit insignificant and less robust), one should point out here that health shocks 28
Table 10: Heterogeneous effects of PROSPERA on young members.

||(1)|(2)|(3)|(4)|(5)|(6)|(7)|(8)|
|---|---|---|---|---|---|---|---|---|
||Transport|Entert<br>eq|Kitchen<br>sup|Basic<br>serv|Y.<br>school|_Inc >_0|log(incom|e)ln(imp<br>cons)|
|**_Panel A: Overall_**|||||||||
|Treatment X 2017|0.0275<br>(0.0272)|0.119*<br>(0.0609)|0.142**<br>(0.0593)|-0.0119<br>(0.0820)|0.0269<br>(0.209)|-0.0194<br>(0.0273)|-0.0736<br>(0.0848)|0.0311***<br>(0.0119)|
|**_Panel B: Household_**|**_status_**||||||||
|Original HH|0.050<br>(0.039)|0.043<br>(0.072)|-0.007<br>(0.072)|-0.042<br>(0.090)|0.221<br>(0.261)|-0.062*<br>(0.038)|-0.113<br>(0.094)|0.001<br>(0.014)|
|New HH|0.009<br>(0.029)|0.174**<br>(0.069)|0.253***<br>(0.072)|0.011<br>(0.088)|-0.130<br>(0.237)|0.028<br>(0.027)|-0.046<br>(0.100)|0.054***<br>(0.014)|
|**_Panel C: Age (in 19_**|**_97) groups_**||||||||
|0-5|0.025<br>(0.032)|0.072<br>(0.075)|0.148**<br>(0.072)|-0.035<br>(0.089)|0.200<br>(0.220)|-0.009<br>(0.035)|-0.043<br>(0.065)|0.022<br>(0.015)|
|6-10|-0.001|0.108|0.019|-0.001|0.167|-0.013|-0.070|0.031*|
|11-16|(0.036)<br>0.057|(0.091)<br>0.329***|(0.085)<br>0.262**|(0.100)<br>-0.017|(0.258)<br>0.711***|(0.036)<br>-0.016|(0.058)<br>0.097|(0.018)<br>0.050**|
|Over 16|(0.048)<br>0.097|(0.101)<br>0.051|(0.112)<br>0.307**|(0.131)<br>0.130|(0.252)<br>-0.043|(0.052)<br>-0.023|(0.166)<br>0.187|(0.021)<br>0.045|
||(0.060)|(0.147)|(0.154)|(0.137)|(0.293)|(0.087)|(0.171)|(0.034)|
|**_Panel D: Health sho_**|**_cks_**||||||||
|No health shocks<br>Health shocks|0.026<br>(0.030)<br>0.031<br>(0.038)|0.178***<br>(0.068)<br>-0.038<br>(0.078)|0.148**<br>(0.066)<br>0.127<br>(0.081)|0.002<br>(0.086)<br>-0.103<br>(0.100)|0.041<br>(0.228)<br>-0.010<br>(0.293)|-0.047<br>(0.031)<br>0.047<br>(0.039)|-0.122<br>(0.092)<br>0.052<br>(0.110)|0.033***<br>(0.013)<br>0.027<br>(0.018)|
|**_Panel E: Migration_**|||||||||
|Same locality|0.043|0.061|0.074|-0.056|-0.086|-0.035|-0.057|0.013|
||(0.031)|(0.068)|(0.068)|(0.087)|(0.232)|(0.032)|(0.102)|(0.012)|
|Mig: Metropolis|0.047|0.477**|-0.043|0.225|0.603|0.031|-0.176|0.047|
||(0.063)|(0.225)|(0.2142)|(0.239)|(0.986)|(0.045)|(0.224)|(0.043)|
|Mig: Other|-0.017|0.227**|0.314***|0.055|0.226|0.007|-0.184|0.061|
||(0.042)|(0.092)|(0.098)|(0.112)|(0.311)|(0.032)|(0.110)|(0.020)|
|Observations|6,702|6,702|6,702|6,702|6,702|5,484|4,794|6,527|
|Mean C 1997|0.020|0.985|0.412|1.218|1.392|0.036|0.237|8.971|
|Mean C 2017|0.220|1.420|1.814|2.483|8.009|0.799|8.118|9.139|

This table shows the possible heterogeneity of the long-term effect for individuals by specific groups of interest. The unit of observation is an individual, who could be in an original or new household. The outcomes constructed are: (1) _Transportation_ , which adds the number of cars and vans; (2) _Entertainment equipment_ , which gathers under entertainment equipment number of TV, radio and sound equipment; (3) _Kitchen supplies_ , which sums the following appliances: blender, refrigerator, electric grill, gas stove or microwave oven; (4) _Basic services_ , which consists of the availability of the following services: firm floor, electricity, drainage and water access in the property; (5) _Years of completed formal schooling_ ; (6) _Pos income_ indicates household per capita income greater than zero; (7) _log(income)_ , is total individual income; and (8) _log(imp cons)_ , is the imputed measure of non-durable expenditure on food personal products, and clothing. Data employed comes from 1997 ENCASEH and 2017-18 ENCEL. Panel A shows a DiD estimation. Panel B estimates the treatment effect for different HH types: original and new. Panel C explores differences in the treatment effect by groups of age formed based on the ages associated to critical schooling stages. Panel D shows differences by health shocks status (health shocks are defined as having at least one household member sick or injured during the two weeks before the survey). Panel E looks into the treatment effect by migration status (Metropolis includes Mexico City, Guadalajara and Monterrey). Controls include (from ENCASEH 1997): HH head age, education, speaking a dialect, HH size, % members under 15, dummies for home, productive land and draft animals ownership, and locality marginalization index. Standard errors clustered at the locality level. Asterisks indicate significance at the ***1%, **5%, and *10% level.

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are seldom fully exogenous so that this is just a tentative correlation analysis. Finally, as shown in Panel E, the positive effects are driven mostly by migrants (but migrants not to the big cities). Interestingly, it seems to be the case that these individuals are doing better in terms of durable assets, but not in income.

# **VI.B.2 Intergenerational Transmission**

In _Table 11_ we show the effects of PROSPERA on intergenerational mobility in terms of divergence of children’s outcomes from their parents, perhaps one of the most relevant aspect of a long-term evaluation. For the new generation, the offspring, still living at home we find relatively little aside from a closing of the gap more pronounced for treated households in terms of income percentile. More interestingly for the newly formed households in Panel B, we find substantial evidence of improvement in the rankings of education, asset holding and income distribution; in fact the results suggest that PROSPERA also improved the general mobility so that not only the children of the better off original households appear to do better but particularly those who started lower in the distribution seem to do better (see the negative sign on the _Treat *Y_ ( _G_ 1) coefficient). These effects are economically relevant and quite encouraging as they show an upward mobility for the beneficiaries, exactly what the program aimed to achieve.

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Table 11: Intergenerational transmission. Convergence / Divergence.

||**Years**|**school**|**Asset ind**|**ex Pctile**|**Incom**|**e Pctile**|
|---|---|---|---|---|---|---|
||(1)|(2)|(3)|(4)|(5)|(6)|
||∆_Y_|∆_Y_|∆_Y_|∆_Y_|∆_Y_|∆_Y_|
|**_Panel A: Original hous_**|**_eholds_**||||||
|_Treat_|-0.282|-0.0788|1.892|-3.000|0.889|-7.220*|
||(0.219)|(0.337)|(1.858)|(2.521)|(2.965)|(3.830)|
|_Y_(_G_1)1997||-0.657***||-0.681***||-0.997***|
|||(0.0636)||(0.0457)||(0.0564)|
|_Treat ∗Y_(_G_1)1997||-0.031<br>(0.0723)||0.092*<br>(0.0520)||0.113<br>(0.0746)|
|Constant|1.270*|6.942***|2.515|38.73***|59.71***|93.42***|
||(0.679)|(0.717)|(6.794)|(5.755)|(8.744)|(7.655)|
|Observations|1,442|1,442|1,432|1,432|939|939|
|R-squared|0.056|0.266|0.027|0.275|0.081|0.486|
|_Mean C Y_(_G_1)1997|2.86|2.86|37.00|37.00|44.24|44.24|
|_Mean C Y_ (_G_2)2017|8.32|8.32|45.04|45.04|56.08|56.08|
|**_Panel B: New househo_**|**_lds_**||||||
|_Treat_|0.298|0.833***|6.918***|4.035|5.950**|6.579*|
||(0.192)|(0.270)|(2.269)|(2.860)|(2.549)|(3.629)|
|_Y_(_G_1)1997||-0.657***||-0.862***||-0.833***|
|||(0.0469)||(0.0436)||(0.0524)|
|_Treat ∗Y_(_G_1)1997||-0.139**||0.014||-0.078|
|||(0.0555)||(0.0572)||(0.0644)|
|Constant|4.061***|8.173***|-16.51**|30.07***|11.61|55.85***|
||(0.705)|(0.625)|(6.932)|(5.891)|(9.296)|(7.894)|
|Observations|1,891|1,891|1,880|1,880|1,354|1,354|
|R-squared|0.089|0.391|0.054|0.357|0.069|0.423|
|_Mean C Y_(_G_1)1997|2.71|2.71|38.89|38.89|42.46|42.46|
|_Mean C Y_(_G_2)2017|7.76|7.76|40.51|40.51|42.36|42.36|

This table analyzes the inter-generational mobility relation to the parent’s (Generation 1, G1) distributional position to understand how poorer or richer households manage to change their distributional position for specific outcomes and how _Treatment_ affects this relation. Inter-generational mobility is defined as ∆ _Y_ = _Y_ ( _G_ 2)2017 _− Y_ ( _G_ 1)1997, where _Y_ ( _G_ 2)2017 and _Y_ ( _G_ 1)1997 are defined as the outcome of the offspring (G2) or parents (G1) observed in 2017 or 1997, respectively. The outcomes of interest considered are: (1) years of schooling; (2) a durable asset index formed with a principal component that considers ownership of cars, vans, TV, radio, sound equipment, blender, refrigerator, electric grill, gas stove, microwave oven, firm floor, electricity, drainage and water access in the property; and (3) monthly income. For column (1) the level of years of schooling is used by itself. For columns (2) and (3), the percentile of each outcome is calculated relative to all the individuals inside the same 10-year window age range. The unit of observation are individuals in relevant age groups, as described in section IV and their parents. Controls include (from ENCASEH 1997): HH head age, education, speaking a dialect, HH size, % members under 15, dummies for home, productive land and draft animals ownership, and locality marginalization index. Standard errors clustered at the locality level. Asterisks indicate significance at the ***1%, **5%, and *10% level.

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# **VI.C DiD Estimates of Program Roll-out**

Our second identification strategy, based on the sequential roll-out of the policy, provides additional evidence and on larger differences in exposure to the program than the experimental variation discussed so far. At the same time, the data employed in this part contain direct measures of food security and vulnerability which add another layer to our welfare analysis. Further to that, we can also test for the effect of PROSPERA on later dependency on governmental programs, this would be a test of a successful policy able to graduate its beneficiaries out of social programs. Our approach here is to produce DiD estimates similarly to Parker and Vogl (2018), but with INEGI’s 2015 intercensus data.<sup>19</sup> _Figure 2_ contains the main estimates of this strategy. Each sub-graph shows the _τ_ estimates from equation (5), which correspond to difference-in-difference estimates. As one moves to the right through the X-axis you increase the exposure to PROSPERA (calculated by comparing 1998 to different delays to enroll) for a given cohort with respect to the cohort that should not be benefited by the program (17-22 year old individuals in 2001).

The results show positive effects on education, particularly for the cohort with the youngest members, which increases their schooling attainment between 0.5 and 1.5 additional years. For the other cohorts, the program involves an increase around 0.5 years of schooling. Regarding income, positive and significant effects are found: household per capita income increases between 2% and 8%, with largest effects for the cohort of those aged 6-10 in 2001. Positive effects are also found for a composite index of house characteristics and durable assets. When analyzing asset by asset, the largest effects are found for type of floor, washer, and cellphone. The largest effects are again found for the youngest cohort. To test for dependency on government aid, or graduation from social programs, we use, as dependent variable, a dummy equal to 1 if the household receives transfers from the government. In this case, overall the evidence suggests that longer exposure to PROSPERA decreases the dependency on government aid. Unfortunately, this measure does not distinguish PROSPERA from other type of government aid. Finally, we look at proxies for vulnerability and food security: two different measures directly addressing food consumption. One question asks whether any adult, in the household, went hungry at least once during the last month. The second question asks whether not enough money was available to purchase enough food variety. We take these two questions as proxies for food security, vulnerability, and quality of the diet. For the younger cohorts we have positive effects on this measure of food security, as those exposed longer are less likely to go hungry (although the estimates are not precise). As for food variety, larger effects are found for the youngest cohort. For them, the likelihood of not being able to buy enough variety decreases between 1 and 2 percentage points for those with longer exposure.<sup>20</sup> These latter two effects on

> 19As explained in section V.B, these estimates are part of our current research where we seek to use an RDD design with the original rule that established that participating localities would be enrolled to the program based on a marginality index.

> 20The food scarcity variables are separately asked for children and adults in the household. Similar estimates

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food security, coupled with the results on aid dependency, suggest that a higher exposure for those most likely to benefit from PROSPERA, with respect to their control counterpart, moved beneficiaries on a higher welfare path. There are clearly some limitations to this approach, not differently from other studies employing DiD strategies. For instance, if more capable individuals from younger cohorts migrate out of poorer locations to a larger extent, our results might reflect a self-selection problem. Parker and Vogl (2018) provide some robustness checks for the selective migration by using each individual’s previous location and noting that PROSPERA does not seem to promote migration in large numbers.<sup>21</sup>

# **VII Conclusions**

We provide an analysis of PROSPERA’s ability to improve the social and economic lives of original households and their offspring. We do so through the lens of the long-term effects of the program on the welfare of its recipients. While the study has some limitations due to the available data, as well as the limited extent of variation in treatment intensity (for the cleanest identification strategy), the long-term effects of PROSPERA are particularly encouraging for the offspring of the originally treated households. These new households, formed by young adults who were themselves direct beneficiaries of the program (when children), present higher ownership of durable assets, and larger non-durable consumption expenditure, suggesting higher welfare. These results are fully consistent with the improved human capital, through the schooling and health effects well documented by the literature on PROSPERA’s short and medium-term effects. Even more importantly, these new households are climbing the economic and social ladder faster than their control counterpart. Their rank, in the relevant distribution, is certainly higher than their parents’ in terms of asset holdings and income, and differentially so for the offspring of the early entrants in PROSPERA. We take this latter result as very exciting evidence of PROSPERA’s ability to put beneficiaries on a positive trajectory and permanently out of poverty. Our results are fully consistent with the existing literature, given the improvements in human capital (health and education), accompanied by higher, and less volatile, income streams through savings and investment in higher returns activities. Ultimately, the success of PROSPERA should be judged upon its long-term (and permanent) effects and on its ability to lift beneficiaries, and their offspring, out of poverty, facilitating their upward mobility on the social and economic ladder. The future direction for these studies is that of acquiring larger and more detailed data to be able to augment the current evidence with other indicators, including directly measuring non-durable consumption, and providing a better understanding of the exact mechanisms behind our findings with the aid of a formal theoretical framework.

> as the ones presented for adults are found for children.

> 21Further work is being done by the authors at the time of writing to tackle these concerns.

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