Impacts of the Bono Juana Azurduy:
An analysis of the effects of a Bolivian conditional cash
transfer program on childhood health outcomes
Catherine MacLeod- 11633549
Master thesis, MSc Economics
July 2018
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STATEMENT OF ORIGINALITY
This document is written by student Catherine MacLeod, who declares to take full responsibility for the contents of this document. I declare that the text and the work presented in this document is original and that no sources other than those mentioned in the text and its references have been used in creating it. The Faculty of Economics and Business is responsible solely for the supervision of completion of the work, not for the contents.
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ABSTRACT
This thesis estimates the effects of a conditional cash transfer (CCT) program on childhood health outcomes in Bolivia. The analysis exploits a discontinuity in eligibility for the Bono Juana Azurduy (BJA), a CCT that provides stipends for attending a predetermined number of doctors’ visits between 0 and 24 months of age, to implement regression discontinuity (RD) and fixed effects analyses. Data from two nationally representative surveys are used to estimate outcomes three and seven years after implementation of the program. While there is some evidence to suggest that eligibility leads to an increase in check-ups attended, there is little to no evidence of significant impacts on childhood health outcomes. These results are generally robust across sharp RD and fixed effects specifications. This is contradictory to much of the literature about the impact of CCTs in developing countries, likely due to the specific nature of the BJA. There is also no evidence to suggest any impact of the program on spacing between children or spillover effects within families.
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Table of Contents
1. I
NTRODUCTION4
2. B
ACKGROUND ANDC
ONTEXT6
3. D
ATA8
i. ESNUT 2012
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ii. ESDA 2016
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4. M
ETHODOLOGY13
i. Regression Discontinuity
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ii. Fixed effects
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iii. Spillover effects
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5. R
ESULTS16
i. Short-term effects
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ii. Long term effects
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iii. Spillover effects
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6. C
ONCLUSION27
R
EFERENCES29
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1. Introduction
Conditional cash transfer (CCT) programs are a popular mechanism for poverty reduction in many developing countries, especially those in Latin America. This thesis will analyze the effect of one particular Bolivian CCT, the Bono Juana Azurduy (BJA), on childhood health outcomes. This will be done using regression discontinuity (RD) and fixed effects designs. Additionally, I will analyze the effects of the program on birth spacing and spillover effects on non-eligible siblings.
The study of CCTs are relevant because they are so widespread throughout the developing world. As of 2010, 129 million people in Latin American countries were recipients of conditional cash transfers. Conditional cash transfers (CCTs) are programs that transfer sums of cash to households for investing in human capital, usually for their children. Transfers are often conditional on participation in education or health activities, such as attending a predetermined amount of school days, receiving certain vaccinations, attending specific numbers of doctor’s visits, and nutrition and growth monitoring. The purpose of many CCT programs is to reduce poverty. They often do so in the short-term with the actual cash transfer and in the long-term by increasing investment in human capital. Payments often average between 10-15% of household consumption (Fiszbein et al. 2009). These types of programs may work through multiple channels, namely both an income effect and a signaling effect. If only the income effect is relevant, conditionality of
the transfer is unnecessary to achieve the desired results1. CCT programs have been
particularly popular in Latin America and the Caribbean (LAC). Seventeen Latin American countries introduced conditional cash transfers between the 1990s and 2010, including Bolivia. Bolivian CCT programs include the Bono Juana Azurduy (BJA), announced in 2009, and the Bono Juancito Pinto (BJP), announced in 2006. The BJA is directed toward expecting mothers and their children under 24 months to increase demand for healthcare services and the BJP is directed toward schoolchildren to increase school attendance. Unlike many other Latin American CCT programs, those in Bolivia were universal (instead of being targeted toward the poor), and the transfer amount was equivalent to about 2-3% of household consumption (in comparison to 10-15%) (McGuire, 2013). The smaller incentive amount of the BJA suggests that the mechanism through which the program affects outcomes is an increased number of doctors’ visits and not an income effect.
Empirical studies have found positive outcomes of CCTs from many programs in the LAC area. Gertler (2004) conducted a randomized controlled trial
1 For evidence of positive benefits of unconditional cash transfers on human
capital outcomes, see Duflo (2003) on old-age pensions and intra-household allocation in South Africa and Haushofer et al. (2016) on the short-term impact of unconditional cash transfers in Kenya.
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(RCT) to investigate the impact of Mexico’s PROGRESA program, which began in 1997. PROGRESA (now Oportunidades) is a CCT issuing transfers every two months for participating in behaviors designed to improve health and nutrition such as prenatal care, well-baby visits, immunizations, preventative check-ups, and participation in educational programs. The paper finds that treated children aged 0-35 months experience a reduction in illness rates of 39.5% after two years in the program. Barham (2011) also studied PROGRESA, using the randomized roll-out to create a treatment variable using the percent of households receiving transfers in a given year and municipality. Barham provides evidence to support that PROGRESA resulted in a 17% decrease in the infant mortality rate amongst the treatment group, with the largest declines in groups for whom the original levels were above the median. Attanasio et al. (2005) analyzed the Familias en Acción program in Colombia with a differences-in-differences approach, finding large and significant positive effects on health outcomes of young children. The program, inspired by PROGRESA, offered a subsidy for mothers to take their children under five years of age to growth and development check-ups. Health outcomes from the Familias en Acción program include increasing preventative healthcare visits by over 20 percentage points, decreasing incidence of diarrhea by 10 percentage points for children under four years of age, and decreasing incidences of stunting (particularly in rural areas). Maluccio et al. (2004) found, based on an RCT made possible by the randomized roll-out of the Nicaraguan Red de Proteccion Social (RPS), that services such as weighing children, updating their health cards, and vaccinations increased while incidences of stunting decreased. This was particularly prevalent amongst the poorest quintiles.
Celhay et al. (2016) studied the BJA in particular, looking at maternal and child health outcomes. This paper uses the ESNUT 2012 survey as well as Bolivian census data. To analyze the effect on stillbirths, the authors use OLS, creating a treatment variable of the percentage of enrolled women in each municipality of Bolivia. They use an approach similar to a difference in differences (DID) design to compare enrolled and non-enrolled pregnancies to estimate effects on maternal outcomes, prenatal outcomes, and birth weight. The paper finds that the program reduced incidence of stillbirths by 38.8%. It also finds that enrolled mothers have their first prenatal check-up significantly earlier than non-enrolled mothers and are 10.3 percentage points more likely to complete four or more prenatal check-ups. They find no significant effects on birth attendance by a skilled professional or birth weight.
When analyzing the effects of the program on childhood health outcomes, the paper opts for a fuzzy RD design. Due to a lack of information in the available data that will be discussed in sections 3 and 4, the paper creates a variable for ‘average weekly participation’. This is done by calculating the average enrollment
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rate in the BJA for each week and assigning this value to all individuals in that particular week. They then use eligibility to instrument for average weekly participation. A fixed effects specification is also applied. The paper finds that using the RD specification, children attend significantly more doctors visits around the magnitude of one and using the fixed effects specification, children were more likely to be vaccinated for yellow fever and measles mumps and rubella. However, they find no further effects on childhood health outcomes due to the BJA.
This thesis adds to the existing literature by providing an analysis of a particular type of CCT program. The BJA differs from traditional CCT programs because the amount of the transfer is less than the traditional amount and the program is universal, not targeted toward the poor. Analysis of a program with these particular features may be useful in the design and implementation of future programs. Celhay et al. analyzed the BJA, however this thesis goes further into the analysis of childhood health outcomes. I look at a wider range of outcomes and use an intent to treat analysis leading to a sharp RD instead of a fuzzy RD design. This is because the analysis using the created ‘average weekly participation’ variable is not completely convincing due to the large amount of missing responses in the data.
The main findings of this thesis are that while the BJA causes children to attend more doctors’ visits, it has little to no significant effects on health outcomes. This is likely because children are already attending a sufficient number of check-ups, and the additional visits have little effect. I also find insignificant impacts on time spacing between children or spillover effects for doctors’ visits of siblings. The finding that this program does not lead to significantly better health outcomes is contradictory to much of the existing literature about the impacts of CCTs in developing countries.
This thesis is structured as follows: section 2 introduces the background and context of the BJA program. Section 3 describes the data used, which are Bolivian surveys from 2012 and 2016. Section 4 discusses methodology. Section 5 presents the results, and section 6 concludes.
2. Background and Context
The Bono Juana Azurduy is a national conditional cash transfer program that was announced in April 2009 by Bolivian president Evo Morales. The program’s main goal was to increase the demand and use of health services for pregnant women and their children under 24 months of age. Mothers could receive separate cash stipends for participating in or receiving numerous medical services such as four prenatal visits, birth being attended by a skilled professional, obtaining a birth certificate for the child, monitoring of the baby for one week after birth, and check-ups once every two months for the first 24 months. Unlike many other
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conditional cash transfer programs, the BJA was not targeted toward the poor; all
mothers covered by Universal and Child Insurance (SUMI) are eligible. SUMI2,
introduced in 2003, is a publicly financed health insurance scheme that covers the cost of necessary maternal and child health interventions. This insurance covers about 80% of mothers and children in Bolivia, not including those covered by private health insurance schemes. Because of this, the Bono Juana Azurduy is not specifically an anti-poverty initiative. Another requirement for eligibility is that mothers must not have given birth to another child within the past three years, as not to incentivize women to get pregnant quickly after a previous pregnancy to receive money from the transfer. To ensure that children will receive benefits from the program for at least one year, eligibility requirements state that children must be enrolled before they are 12 months old. Due to this requirement, when the program was announced in 2009, only children born after May 2008 could receive benefits from the BJA transfer, creating a natural discontinuity in eligibility.
Between 2009 and 2012, approximately 33% of eligible women and 52% of eligible children were enrolled in the BJA (Celhay et al., 2016). The main reasons eligible mothers did not enroll themselves or their children included not knowing about enrollment procedures and not having the necessary documents to enroll, which included a national identification card for the mother and birth certificate for the child.
The portion of the program focused on check-ups for children under two years of age provided the mother with a 120 boliviano stipend for each check-up she brought her child to (equivalent to about 17 USD), which is a small-scale transfer in comparison with most other conditional cash transfer programs. If the mother received all of the money she was eligible for during and after a given pregnancy, the total amount is equal to about 260 USD, or 3% of the average yearly household consumption of a Bolivian family over the 33 eligible months (through pregnancy and the first 24 months the child is alive). However, as the BJA was not focused on the poor, this measurement is for the average Bolivian family and the transfer would likely be much more significant in the lives of those families living
in poverty3. The program is funded in part by the World Bank, the Interamerican
Development Bank, and the Bolivian National Treasury through the nationalization
of natural resources4.
2 Children in Bolivia have been covered by universal healthcare before 2003-
beginning in 1997 with the Maternal and Child insurance(NMN), continuing in 1998 with Basic Health Insurance (SBS), and continuing with SUMI in 2003. Intensity and complexity of services covered has increased over time.
3 According to World Bank data, the poverty headcount ratio in Bolivia in 2009
(measured on US $1.90 a day at 2011 PPP) was 10.5% of the population.
4 This includes nationalization of hydrocarbons in 2006 and increases in taxes on
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During the implementation of the BJA, payment centers were heavily relied on to manage the cash transfers. In urban areas, the payment centers were branches of two national banks in Bolivia. In rural areas or communities without a branch, payment was often taken care of by the armed forces, which was less reliable. If there was no payment center in a particular municipality, the mother had to travel to the nearest municipality with a payment center. However, the exact location they could receive the transfer was somewhat unclear. Celhay et al. (2016) exploited the role of payment centers to analyze the effects of the BJA finding significant effects on prenatal outcomes but few effects on childhood health outcomes, as discussed in the introduction.
The channels through which the BJA affects birth outcomes are through receiving the proper number of prenatal doctors’ visits. Evaluation of the pregnancy risk level and monitoring the progress along with information about risk signs, nutrition, and immunizations should lead to positive effects on birth outcomes and decrease early neonatal mortality, which studied in depth by Celhay et al. (2016). Following this example, the main focus of this thesis will be on childhood health outcomes. The small incentive amount of this program suggests that the channel through which the transfer has an effect on childhood health is not likely through an income effect, but an encouragement effect that encourages mothers to attend the proper number of check-ups. If the child is taken for a sufficient number of doctors’ visits, they should receive help for issues they may
encounter at a young age5 or medication/vaccinations for any avoidable illnesses.
It is also likely that at the doctors’ visits, the parents will receive information about how to best care for their children and will be able to apply this information in the home even after the first 24 months, leading to long-term positive outcomes.
3. Data
The main sources of data used in this paper are surveys completed by Bolivian government agencies. The first survey is the Health and Nutrition Evaluation Survey (ESNUT, by Spanish acronym) from 2012, completed by the Unit for the Analysis of Social and Economic Policies in cooperation with the Bolivian Ministry of Health. The second survey used is the 2016 Demographic and Health survey (EDSA, by Spanish acronym), completed by Bolivia’s National Institute of Statistics.
5 Multiple studies have shown that health interventions in early childhood may
have large returns later, including Attanasio et al. (2015), Gertler et al. (2013), and Macours et al. (2012).
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i. ESNUT 2012
The ESNUT survey is a nationally representative household survey that was conducted in 2012 with the objective of providing updated information on the health conditions and nutritional status of the population. The survey focuses on women of childbearing age and children under five years of age. Data was collected from over 11,000 children under five years of age and over 12,000 women between 14 and 49 years of age. Unlike data available from Bolivia’s national health information system, this survey collects data from those who are registered under certain health insurances and receive services as well as those who are not. Data from the ESNUT 2012 provides the frequency, distribution, and characteristics of health conditions, information on the use of services, and coverage of national programs, starting from a representative sample of the population of households with small children throughout the country. The survey also contains information on the socio-demographic and economic characteristics of households and their members, health status, healthy habits, maternal health, child health, nutrition in girls and boys under five, anthropometric measurements, hemoglobin levels, deficiencies of vitamin A and iron, and use of preventive maternal and child health services. Data was collected through interviews with individuals at their homes. Though the survey was done in part to analyze programs such as the BJA, the dataset does not provide comprehensive information regarding who was registered for the program. Though ‘participation in the BJA’ is asked in the survey, only about 3.4% participants responded. Because of this lack of data, the main analysis will be based on an intention to treat (ITT) framework.
ii. ESDA 2016
The objective of the ESDA, conducted in 2016, was to evaluate public policies of the health sector and establish new strategies, plans, and programs that will better serve the population. This is also a nationally representative and obtains information from women between the ages of 14 and 49 (regarding themselves and their children) and men aged 15 to 64. The women in the survey are asked about current and previous pregnancies as well as the health of their children. The full sample contains 15,160 households spread across Bolivia’s eight districts. Data from the ESDA provides information about child and maternal nutritional status, fertility and infant mortality rates, as well as other indicators of reproductive health and family planning. Surveys were completed at the homes of individuals on electronic tablets in three sections: home, women, and men and anthropologic measurements were taken at the time of the survey. This data set does not contain information on what types of health insurance the households or mothers are registered under or usage of certain health services, such as check-ups. The data
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also does not provide comprehensive information about which individuals were registered for the BJA.
Descriptive statistics are displayed below in Tables 1 and 2. Information from both the 2012 ESNUT and 2016 ESDA surveys provide evidence to suggest that there are few to no significant differences between those children who were eligible for the program and those who were not eligible. Odd numbered columns present the means for the control group, the non-eligible children, with the number of observations in the control group. Even numbered columns present the differences, by control group mean minus treatment group mean, with the number of observations in both groups combined. The 2012 data contains no significant differences whatsoever between the treatment and control groups. The 2016 data shows that when using a bandwidth of one year, the control group is significantly more likely to live in the district Oruro at the 5% level, however this difference disappears as the bandwidth becomes smaller.
Table 1: Descriptive statistics, 2012
(1) (2) (3) (4) (5) (6)
means 365 days means 182 days means 91 days
control control control
Mother’s schooling 6.730 0.024 6.421 -0.353 6.359 -0.495
(0.200) (0.245) (0.352)
Mother’s age at birth 27.114 -0.052 27.122 0.308 27.293 0.871
(0.334) (0.417) (0.596)
Schooling of household head 7.515 0.257 7.109 -0.226 7.056 -0.327
(0.195) (0.236) (0.320)
Total annual expenditure 2460.243 153.800 2381.693 132.224 2357.161 168.624 (100.500) (127.600) (139.622) Annual food expenditure 1426.151 17.800 1411.854 50.188 1370.316 53.677
(69.290) (88.700) (82.532) Distance from nearest health clinic 3.282 -0.337⇤ 3.535 -0.116 3.666 0.042
(0.178) (0.220) (0.303)
Gender, female=1 0.510 0.004 .502 -0.009 0.530 0.001
(0.022) (0.027) (0.039)
Check-ups between 0-6 months 2.641 -0.054 2.639 0.020 2.707 0.071
(0.054) (0.062) (0.086)
N 794 2212 631 1339 321 671
Notes: This table shows the means of the control group and the di↵erence in means for eligible versus non-eligible children of descriptive statistics. The data is a sample from the 2012 ESNUT survey. Columns represent di↵erent bandwidths in days, as indicated in the table. Standard errors are in parentheses.
Table 2: Descriptive statistics, 2016
(1) (2) (3) (4) (5) (6)
means 365 days means 182 days means 91 days control control control
Area (urban=1) 0.533 -0.011 0.550 0.012 0.559 0.016 (0.021) (0.029) (0.040) Poverty level 2.856 -0.050 2.914 0.050 2.940 0.044 of municipality (0.049) (0.067) (0.093) Mother’s education 2.574 0.020 2.599 0.020 2.599 -0.015 (0.039) (0.053) (0.075) Mother’s age at birth 26.536 -0.278 26.770 -0.240 26.576 -0.676
(0.291) (0.407) (0.562) Gender (female=1) 0.467 -0.021 0.461 -0.029 0.462 -0.029
(0.021) (0.028) (0.040) Department (Chuquisaca=1) 0.087 0.011 0.084 0.003 0.084 0.007
(0.011) (0.016) (0.022) Department (La Paz=1) 0.182 0.001 0.175 -0.014 .174 0.000
(0.016) (0.022) (0.030) Department (Cochabama=1) 0.141 -0.008 0.147 -0.020 0.147 -0.030 (0.015) (0.021) (0.029) Department (Oruro=1) 0.097 0.024⇤⇤ 0.086 0.015 0.099 0.029 (0.012) (0.015) (0.022) Department (Potosi=1) 0.135 -0.005 0.115 -0.019 0.114 -0.010 (0.014) (0.019) (0.026) Department (Tarija=1) 0.067 0.003 0.078 0.018 0.066 0.019 (0.010) (0.015) (0.019) Department (Santa Cruz=1) 0.165 -0.022 0.183 0.001 0.171 -0.040
(0.016) (0.022) (0.031) Department (Beni=1) 0.080 -0.005 0.089 0.026 0.087 0.024
(0.011) ( 0.026) (0.021)
N 1156 2354 618 1222 333 632
Notes: : This table shows the means of the control group and di↵erence in means of eligible versus non-eligible children of descriptive statistics. The data is a sample from the 2016 ESDA survey. Columns represent di↵erent bandwidths in days, as indicated in the table. Standard errors are in parentheses.
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4. Methodology
i. Regression Discontinuity
As mentioned previously, the BJA was a national level conditional cash transfer program rolled out in 2009. The eligibility requirements for enrollment of children in the program state that in order to benefit from the program, children must be 12 months of age or less at the time of announcement. This requirement creates a natural discontinuity in eligibility and allows for the use of a regression discontinuity (RD) design. June 1, 2008 is used as the cut-off date, as those born before the date were not eligible to enroll in the program but those born after that date were eligible. Enrollment in the program is not 100% after the cut-off date, which would make a ‘fuzzy’ RD design the most accurate type of analysis. Due to lack of information in the available data, the majority of the analysis will be based on an intention to treat (ITT) framework, and a sharp RD design will be implemented.
In the case of the RD design, it is assumed that probability of treatment is a discontinuous function of some continuous variable relative to a particular cutoff. In the fuzzy design, this discontinuity can then be treated as an instrumental variable. The identifying assumption for using RD is that assignment is ‘as good as’ random, and the interval around the cutoff point should be small enough so that individuals to the right are not systematically different from individuals to the left. In the case of varying treatment effects, estimates will be most relevant for individuals around the cut-off who would be moved into treatment due to the age specific rule. The resulting estimate is a local average treatment effect (LATE). (Van Der Klaauw, 2002)
To formally explain this methodology, let Bi be the birth date of person i,
in days elapsed from June 1, 20086 and Zi be a dummy variable for whether or not
the child is eligible, based on the value of Bi. Let Ei be a dummy variable equal
to 0 if the child is not enrolled in the BJA and 1 if the child is enrolled and let Yi be
outcome variables. The mechanism through which the program should effect
outcome variables is through an increased number of doctors’ visits. Xi is a vector
of control variables for each individual. The IV equations that would be estimated in the fuzzy RD design are equations (1) and (2).
!" = $ + &'" + ()*+ ," (1)
0" = 1 + 2!" + ()*+ 3" (2)
6 With the cutoff of June 1, 2008 being the value 0, meaning that all days to the
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The available data contains problems regarding measurement of Ei
(enrollment in the BJA). Because of this, a sharp RD design is implemented with only one equation (3). In the case of the sharp RD design, individuals are assigned
to the treatment and control groups based only off Bi, their birth date, which makes
Zi equal to 1 if Bi is above the cutoff and 0 if below.
0" = 5 + 6'" + ()" + 7" (3)
This intention to treat analysis simply uses eligibility as the independent variable, and the estimates are the effect of eligibility for the BJA rather than participation in the BJA itself. Because increasing the interval around the cutoff can create bias in the estimations, I estimate the results for health outcomes for three intervals: one year (365 days), half of a year (182 days), and a quarter of a year (91 days). The analysis using the 2012 ESNUT survey estimates the effect of eligibility on short-run outcomes, namely the number of check-ups attended, growth indicators, and vaccinations. Anyone not covered by SUMI insurance is also dropped from the 2012 analysis, as they were not eligible to receive the transfers. The 2016 ESDA survey is used to estimate longer-term outcomes, namely chronic health issues. This dataset does not contain information about the health insurance scheme each individual was covered under, so it is not possible to restrict the sample to only those covered by SUMI.
This RD design is also used to estimate the effect of the program on birth spacing. Recall that one of the requirements for eligibility is that the last child must have been born at least three years prior to receive benefits, as to not incentivize women to get pregnant again quickly. For this analysis, I use a cutoff birth date of February 1, 2010, nine months after the announcement, as this is the first date a potential pregnancy could be affected by the eligibility criteria. The 2016 ESDA survey is used and two outcomes are estimated: days between births of children in a family and the probability of children being three or more years apart. Bandwidths used for this analysis are two, four, and six years, however only the right side of the cutoff (second child born after February 1, 2009) are used. This is because I am only interested in pairs in which at least one child was born after the cutoff. If both children were born before the cutoff, there would be no possibility to be eligible for the BJA.
ii. Fixed effects
In addition to the RD design, I implement fixed effects regressions by household, using a subsample of the data in which one child in the household is eligible for the BJA and one is not. The analysis using the ESNUT 2012 for short-term outcomes consists of children born between 2007 and 2010. Children who are
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not yet 24 months at the time of the survey are dropped because they have not yet received the full treatment and therefore may still be reaping the benefits. In the analysis using the 2016 ESDA for long-term outcomes, children born between 2004 and 2012 are used. This allows for children to be up to eight years apart from each other. I do not use the entire sample from 2000 to 2016 because children that are more than eight years apart are likely to experience systematic differences in upbringing, even if they are part of the same family.
To eliminate the unobserved fixed component of upbringing that is the same across families and thus in an attempt to reduce bias that would be present with OLS, I estimate a fixed effects model comparing the same outcomes across different children in the same family. Consider equation (4), where subscript i
refers to each individual and subscript f refers to a family. Formally, let Yif be the
outcome for individual i in family f. Let Zif be a binary variable that equals 1 if the
individual is eligible for the BJA and 0 if not, Xi is a vector of control variables
specific to individual i and 9: are unobservable fixed variables for families.
0": = ; + <'":+ ()*+ =>:+ ?" (4)
Variables specific to individual i are variables that may change between children in the same family, including mother’s age at birth, mother’s education, birth order of the child, and the child’s age. The unobservable fixed variables for families may include wealth, parenting skills, etc. Estimation by OLS will produce biased results because unobserved characteristics of the family and parenting will likely have an influence on outcomes.
In theory, assuming treatment status is uncorrelated with the unobservable,
this would give an unbiased estimate of the effect of eligibility for the BJA. The identifying assumptions for this approach are that within households, the children who were eligible for the program were not different from those who were not, other than in their eligibility status. If parents systematically treat children differently based on unobservable characteristics, the approach would no longer be valid. The approach also assumes that parents allocate resources equally to each of their children, regardless of gender and birth order. While evidence of differing
treatment by gender exists but does not seem to be present in the LAC area7,
evidence of differing treatment due to birth order appears to be robust across
7 Evidence of differing treatment of boy and girl children in developing countries
has been found, particularly in India (see Rose (1999), who found that favorable rainfall shocks in childhood increased the probability of girls’ survival until school age relative to boys.) However, there is no evidence that this behavior is present in Latin American countries.
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regions and is likely a factor in the sample used8. This may decrease the validity
of the fixed effects analysis, as children who were not eligible are always higher in the birth order than those who were. The fixed effects approach is used to estimate the same outcomes as are looked at in the RD design.
iii. Spillover effects
In addition, I estimate spillover effects of having a sibling eligible for the BJA on the number of doctors’ visits attended by their non-eligible sibling. The theory behind this analysis is that because check-ups are already covered by insurance, mothers taking their eligible child to a check-up with plans to receive the cash transfer will also likely bring their non-eligible child along, as there is no
additional cost9. This is estimated using OLS with equation (5).
0" = ? + AB" + ()" + C" (5)
Let Wi be a dummy variable equal to 1 if individual i has a sibling eligible for
the BJA and 0 if not. The outcome, Yi, is number of check-ups between 12 to 24
and 0 to 24 months. For this specification, only a sample of children born before May 1, 2008 is used. This analysis uses data from the 2012 ESNUT survey, as this survey contains data about number of check-ups. There is, however, a downside to the analysis that there is no information about number of check-ups after two years of age.
5. Results
The main results of this thesis are that the BJA had few significant effects on health outcomes. Main results can be found in Tables 3 and 4. One of the reasons eligibility for the BJA may have had such little effect on short or long-term health outcomes is that children were already attending an adequate number of check-ups. The mean number of check-ups attended between 12 and 24 months for the control was already about five out of a possible six (if the child attends a check-up every two months). While the increase in number of check-ups was significant when
8 Evidence of differing treatment and allocation of resources based on birth order
has been found fairly universally. See Price (2008), who finds that the first child receives on average 20-30 more minutes of quality time with parents each day, and Behrman et al. (1986), who finds that first born children have higher levels of schooling and earnings, apparently due to an endowment effect that overtakes parental preferences or pricing effects.
9 There is no cost for childhood check-ups under the SUMI health insurance,
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using the RD specification, the magnitude is small, ranging from an increase of 0.6 to 0.8 for a one-year period. This small increase was likely not enough to significantly impact other childhood health outcomes. Other findings include a lack of spillover effects and no significant effect on birth spacing.
i. Short-term effects
Figures 1 and 2 are graphical representations of the effects of BJA eligibility on number of doctors’ visits attended. These can be interpreted as the ‘first stage’ results, as increased number of check-ups is the mechanism through which health outcomes should be improved. Figure 1 displays the effect of BJA eligibility on the number of check-ups attended between 12 and 24 months, while Figure 2 illustrates the jump in total check-ups between 0 and 24 months. These graphs represent children born within one year of the cutoff date. Both figures show a clear increase in check-ups attended, though the increase is only of about one visit. Figure 1 is more relevant than Figure 2 as the interval around the cutoff decreases because at the time of announcement of the BJA, children under 12 months could be enrolled. They could not back-date the transfer, so there is no reason for their number of check-ups between 0 and 12 months to be affected by the program for those born at the cutoff. The number of check-ups between 0 and 12 months becomes increasingly relevant as the interval around the cutoff increases.
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Main results for the effect of eligibility on health outcomes based on the 2012 ESNUT survey are presented in Table 3. Columns (1), (2), and (3) present the results from the sharp RD analysis, with each column representing a different
bandwidth10. Columns (4) and (5) present the results from the fixed effects
analysis.
Eligibility for the BJA caused children to attend more doctors’ visits in the periods of 12 to 24 and 0 to 24 months, significantly in the RD specification over all bandwidths, but insignificantly with a fixed effects specification. The reason some outcomes have much more observations than others is due to missing data; parents did not provide answers for certain questions. In the 2012 ESNUT survey, the number of observations for certain vaccines (namely BGC, polio, rotavirus, and yellow fever) are much lower than other outcomes. If those individuals who did not report on these were systematic, this could lead to bias estimates of the effect of eligibility on the program on these outcomes. There are very few other significant results with the exception of increased likelihood to receive the tetanus vaccine and surprisingly, higher incidences of stunting in the RD design. When regressing age on incidence of stunting and height for age with OLS, estimates show that age decreases incidence of stunting and increases height for age, robust with and without controls. A possible explanation for the finding of a higher incidence of stunting in eligible children may be that younger children in Bolivia tend to be chronically more stunted and incidence of stunting decreases as age increases, as is supported by OLS regressions. This would cause the RD design to show more stunting as a result of eligibility because by design it is comparing older to younger children. However, the reason stunting incidence decreases with age in this sample is unclear and difficult to distinguish.
These final regressions do not control for the running variable of age. When including this as a covariate, the effects are extremely small in magnitude, with a magnitude of about .0001, and insignificant. In the RD specification, this is likely because of the nature of the RD design and the fact that the children in the sample are very close in age- the maximum age differences are 2 years to .5 years depending on bandwidth.
10 Bandwidths are one year (365 days), half of a year (182 days), and a quarter of
Table 3: E↵ects of BJA on health outcomes
(1) (2) (3) (4) (5)
365 days 182 days 91 days FE FE Check-ups, 12-24 mo. 0.688⇤⇤⇤ 0.805⇤⇤⇤ 0.621⇤⇤ 0.130 0.439 (0.161) (0.120) (0.273) (0.207) (0.494) N 2044 1232 617 515 493 Clusters - - - 257 244 Check-ups, 0-24 mo. 1.050⇤⇤⇤ 1.031⇤⇤⇤ 0.620⇤ 0.672⇤ 0.758 (0.258) (0.318) (0.446) (0.356) (0.788) N 2030 1218 611 511 490 Clusters - - - 255 245
Height for age -0.123⇤⇤⇤ -0.176⇤⇤⇤ -0.226⇤⇤⇤ -0.355⇤⇤⇤ -0.028
(0.045) (0.055) (0.081) (0.078) (0.170) N 2033 1219 605 511 485 Clusters - - - 255 242 Stunted 0.048⇤ 0.063⇤ 0.083⇤⇤ 0.149⇤⇤⇤ 0.035 (0.019) (0.024) (0.034) (0.035) (0.078) N 2033 1219 605 526 500 Clusters - - - 262 250
Weight for height 0.011 0.024 0.039 0.006 0.016 (0.046) (0.054) (0.073) (0.113) (0..167) N 1911 1036 554 489 465 Clusters - - - 244 232 Tetanus vaccine 0.046⇤⇤ 0.056⇤⇤ 0.046 0.063⇤ 0.022 (0.019) (0.024) (0.033) (0.035) (0.068) N 1823 1080 539 526 439 Clusters - - - 262 219 BCG vaccine -0.010 -0.006 -0.013 - -(0.008) (0.009) (0.016) - -N 627 383 211 - -Polio vaccine 0.005 0.022⇤ 0.028 - -(0.013) (0.013) (0.022) - -N 625 382 211 - -Rotavirus vaccine 0.039 0.024 -0.009 0.160⇤ 0.101 (0.024) (0.028) (0.039) (0.073) (0.124) N 592 362 200 104 104 Clusters - - - 52 52
Yellow fever vaccine -0.012 0.013 0.019 0.120⇤ 0.154
(0.023) (0.028) (0.038) (0.066) (0.102)
N 603 371 203 106 106
Clusters - - - 53 53
Mother fixed e↵ects No No No Yes Yes Control for covariates Yes Yes Yes No Yes
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Though mostly insignificant, the magnitudes and signs of the coefficients are fairly robust across bandwidths and specifications (RD and FE). The exception is that the effect of eligibility on the rotavirus vaccine and yellow fever vaccine are estimated as higher and more significant when using the fixed effects specification without controls. At first this may seem unusual. If a mother is taking one child to the doctor to receive a certain vaccine it is likely that they will bring any other children they have as well. The fact that the fixed effects results are of a higher magnitude than the RD suggests that this is not the case. The explanation for this may be that doctors advocated more heavily for vaccines in later years, particularly following the implementation of the program. This would be noticeable over the two designs because the fixed effects design considers a wider age range of children, while the RD design only considers children within a certain interval around the cutoff. Because the results become insignificant with the addition of fixed effects in column (5), another likely explanation is that other control variables are more responsible for reception of vaccinations.
The reason why few significant impacts are found is likely that children were already attending enough check-ups to receive the benefits that they provide. The marginal increase in visits would then make little difference in treatments or benefits received. Appendix C shows the sharp RD results of health outcomes with controls for a bandwidth of 182 days. The estimates indicate that living in an urban area as has a negative and significant effect on many outcomes. An increase in total number of members in the family has a significant negative effect on check-ups attended. The fact that living in an urban area has a significant and negative effect may be signaling a larger problem with the supply side of healthcare in urban areas in Bolivia. This may include chronic overcrowding of urban clinics and doctors’ offices and a lack of sufficiently trained medical professionals.
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ii. Long term effects
The main results of eligibility on long-term health outcomes using the 2016 ESDA survey are displayed in Table 4. The first three columns present results from RD estimations with bandwidths of 365, 82, and 91 days, respectively. Columns (4) and (5) present results from the fixed effects specification, with and without controls. There are much fewer observations for some outcomes than others, namely respiratory problems, a mental or physical disability, and have had diarrhea in the last 6 months, because mothers often did not respond to every question in the survey. In this case, the first few outcomes were in a different section of the survey which was often not completed.
I find no significant effects of eligibility on long-term outcomes. The RD and fixed effects estimates are generally of the same sign and magnitude, and the sign of the majority of the coefficients is negative, signaling that eligibility may have led to a lower probability of chronic health issues. However, the estimates are very small and only very few are close to significance at any level. The results for the regression discontinuity specification with covariates for a bandwidth of 182 days is shown in appendix D, which shows little impact of any of the covariates on long-term health outcomes. It is possible that the estimated outcomes are not comprehensive, and some positive long-term outcomes were not realized. For a more comprehensive analysis, it would be beneficial to have information about
stunting and illnesses over the past few years11. The 2016 data does not contain
information regarding uptake of the program or doctors’ visits the children attended at a young age, so it is not possible to test a fuzzy RD design as well.
Table 4 : E↵ects of BJA on long-term health outcomes
(1) (2) (3) (4) (5)
365 days 182 days 91 days FE FE Has respiratory problems 0.024 -0.026 -0.088 0.060 0.035
(0.048) (0.065) (0.091) (0.037) (0.070)
N 421 222 119 1250 1103
Clusters - - - 619 528
Has a physical or mental disability. -0.009 -0.015 -0.015 -0.006 -0.003 (0.009) (0.017) (0.024) (0.006) (0.010)
N 419 222 119 1247 1103
Clusters - - - 618 528
Has had diarrhea in last 6 months -0.014 -0.020 -0.002 0.048 -0.056 (0.033) (0.049) (0.062) (0.030) (0.054)
N 421 222 119 1250 1106
Clusters - - - 619 529
Has problems physically moving -0.001 -0.006⇤⇤ -0.004 -0.001 -0.002 (0.002) (0.003) (0.004) (0.002) (0.003)
N 1991 1054 545 6045 5201
Clusters - - - 2556 2260
Has seeing problems -0.001 -0.004 -0.007 -0.003 0.001 (0.003) (0.004) (0.005) (0.002) (0.004)
N 1990 1053 545 6024 5198
Clusters - - - 2556 2260
Has hearing problems 0.000 0.002 0.008 0.000 0.010⇤⇤⇤
(0.002) (0.004) (0.005) (0.001) (0.004)
N 1991 1054 545 6044 5200
Clusters - - - 2546 2260
Has speaking problems -0.002 -0.004 0.033 0.001 0.002 (0.004) (0.005) (0.022) (0.003) (0.005)
N 1991 1054 545 6044 5200
Clusters - - - 2556 2260
Has a learning disability 0.000 -0.006 0.001 -0.004 0.002 (0.003) (0.029) (0.007) (0.003) (0.004)
N 1991 1054 545 6039 5195
Clusters - - - 2556 2260
Mother fixed e↵ects No No No Yes Yes
Control for covariates Yes Yes Yes No Yes Notes: This table shows estimates for the e↵ect of BJA eligibility on long-term health outcomes. Columns (1) (2) and (3) are from a regression discontinuity (RD) analysis and columns (4) and (5) are from a family fixed e↵ects analysis. The regressions control for area (urban/rural), poverty level of the municipality, mother’s education level, and mother’s age at birth in columns (1) (2) and (3) and age, birth order, mother’s age at birth, and mother’s education in (5). Outcome variables are reported in dummy variables for 0 if no and 1 if yes. The data is a sample from the 2016 ESDA survey. Columns (1) (2) and (3) represent samples of di↵erent bandwidths (as shown), and columns (4) and (5) use a sample born between 2004-2012. Standard errors are in parentheses, and those in columns (4) and (5) are clustered at the mother level.
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RD estimations also show that eligibility for the BJA has no significant effect on the space between children. As the interval around the cutoff becomes smaller, the magnitude of the estimate becomes larger, though still insignificant. The bandwidths used in the analysis are 6, 4, and 2 years. Results are displayed in Table 5.
The estimates show that mother’s schooling and mother’s age at the eligible child’s birth significantly increases spacing between children when the outcome is measured in days and in probability of children being three years apart or more.
Living in a municipality with a lower level of poverty12 increases the space between
children and the probability they are born three or more years apart. A possible reason that there was no impact of the program on birth spacing may have been because the average space between children in the control group was 2.8 years. When limiting the sample to pairs in which the second child was born within four years of the implementation of the program, 46% of pairs were born three or more years apart. This gap between children suggests mothers were already making conscious decisions regarding birth spacing.
iii. Spillover effects
Table 6 presents the estimates of spillover effects of check-ups. The results imply that having a younger sibling eligible for the BJA had no significant effect on the number of doctors’ visits attended by their older sibling when measured between 0 and 12 or 0 and 24 months.
The results provide evidence that an increase in mother’s age at child’s birth
and mother’s schooling13 increase total number of check-ups, while increasing
distance to the nearest health center has a small but negative effect (significant only for 0 to 24 months). The reason behind the finding that there are no spillover effects of the BJA on sibling’s doctors’ visits is not distinguishable. Recall the eligibility rule that children must be at least three years apart to be eligible for the transfer. Because the data only reports on doctors’ visits between 0 and 24 months, the estimates would only capture true spillover effects of eligibility if the second child was born within two years of the first. The finding of no significant effect could either mean that the eligibility rule was strictly enforced and that children who were born less than three years apart did not receive the transfer, or that the rules were not strictly followed and there were truly no spillover effects.
12 Poverty level is reported on a scale of 1-5, 5 as the lowest level of poverty and
1 as the highest. Estimates show that a decrease in the poverty level (an increase in the value on the scale) leads to children being born further apart.
13 The effect of mother’s schooling is only significant over total check-ups
between 0-24 months and has an insignificant effect on check-ups between 12-24 months.
Table 5: E↵ects of BJA on birth spacing
Days apart 3 Years Apart
(1) (2) (3) (4) (5) (6)
2190 days 1460 days 730 days 2190 days 1460 days 730 days Younger child potentially -21.398 11.289 68.878 -0.002 0.024 0.044 eligible for BJA (30.585) ( 35.359) (57.856) (0.016) (0.026) (0.037) Mother’s schooling 118.858⇤⇤⇤ 123.861⇤⇤⇤ 141.54⇤⇤⇤ 0.089⇤⇤⇤ 0.068⇤⇤⇤ .086⇤⇤⇤
(11.421) (12.342) (18.564) (0.016) (0.008) (0.011) Poverty level of 65.157⇤⇤⇤ 73.755⇤⇤⇤ 76.987⇤⇤⇤ 0.031⇤⇤⇤ 0.039⇤⇤⇤ 0.035⇤⇤⇤
municipality (7.284) ( 7.931) (11.864) (0.004) (0.006) (0.008) Mother’s age at birth 25.536⇤⇤⇤ 26.828⇤⇤⇤ 29.606⇤⇤⇤ -0.002⇤⇤ 0.014⇤⇤⇤ 0.014⇤⇤⇤
( 1.661) ( 1.752) ( 2.443) (0.001) (0.001) (0.001) Birth date of younger child 0.190⇤⇤⇤ 0.161⇤⇤⇤ 0.108 0.000 0.000 0.000
(.020) (.0173) (.068) (0.000) (0.000) (0.000) Constant 145.715⇤⇤ 53.015 -98.477 0.402⇤⇤⇤ -0.018⇤⇤⇤ -0.225⇤⇤⇤
( 60.879) (64.617) ( 92.653) (0.026) (0.042) (0.058)
N 7027 6158 2805 7027 6158 2805
Notes: This table shows the e↵ect of eligibility for the BJA on birth spacing. Columns 1, 2, and 3 report on the outcome variable ’days apart’, and columns 4, 5, and 6 report on an outcome variable for 1 if the children are 3 years apart or more and 0 if not. ’Younger child eligible for BJA’ is a dummy variable of 1 if the younger child in a pair is eligible and 0 if not. Poverty level of the municipality is defined on a scale of 1-5, 1 being the poorest and 5 being the least poor. The data is a sample from the 2016 ESDA survey. Columns represent di↵erent bandwidths, as shown. Standard errors in parentheses
Table 6: Spillover e↵ects of BJA for siblings doctors visits
(1) (2)
Check-ups, 12-24 months Checkups, 0-24 months Had sibling eligible 0.198 0.118
for BJA (0.222) (0.348) Mother’s age 0.037⇤⇤⇤ 0.052⇤⇤⇤ at birth (0.012) (0.020) Mother’s schooling -0.001 0.083⇤⇤ (0.021) (0.034) Distance to nearest -0.026 -0.075⇤⇤⇤ health center (0.018) (0.028) Constant 4.926⇤⇤⇤ 12.83⇤⇤⇤ (0.479) (0.750) N 2193 2177
Notes: This table shows estimates of spillover e↵ects of eligibility for the program, namely if having a sibling eligible for the BJA increased the num-ber of doctors visits for their older siblings in comparison to their counter-parts without an eligible family member. ”Had sibling eligible for BJA” is a dummy variable of 1 if the child had an eligible sibling and 0 if not. The sample is only children born before May 1, 2008. Standard errors in parentheses.
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6. Conclusion
This thesis uses fixed effects and regression discontinuity designs to estimate the effect of a Bolivian conditional cash transfer, the Bono Juana Azurduy, on childhood health outcomes. The validity of the regression discontinuity analysis depends upon the assumption that those born just before the cutoff from the program are not systematically different than those born after, other than in eligibility status. Means testing for descriptive statistics for both the 2012 and 2016 data show few to no significant differences in characteristics, affirming this assumption. The sharp RD analysis is dependent on the interval around the cutoff that is used. I estimate outcomes with bandwidths of 365, 182, and 91 days. There is a trade-off in this analysis because as the interval around the cutoff decreases, bias should decrease, however as the interval decreases, the amount of useful observations also decreases. The second strategy, fixed effects, relies on the assumption that within families, parents treat all siblings the same and allocate resources to siblings equally. Findings are that while the BJA increases the number of doctors’ visits attended by eligible children by between 0.6 to 0.8 in the RD specification, it has little to no effect on other short or long-term health outcomes. This increase in check-ups, however, is not significant in the fixed effects specification, so I am unable to draw definitive and robust conclusions. If it is assumed that eligibility truly did increase check-ups, the lack of effects on health outcomes may be because children are already attending an adequate number of check-ups and receiving the maximum benefits. I also find insignificant effects of the three-year apart eligibility rule on birth spacing as well as insignificant spillover effects.
These findings are contradictory to much of the existing literature on CCTs, especially in Latin America. A possible reason for this is the nature of the BJA, as it is different from the archetypal CCT program. The program did not target the poor therefore 80% of mothers and children were eligible at the announcement. The program could have potentially been more effective if it had targeted the poor or if supply-side reforms/expansions had been enacted alongside the program, particularly in urban areas.
Lastly, it is notable to mention the shortcomings of this analysis. The data does not contain comprehensive information regarding uptake of the program. While a fuzzy RD design using take-up of the program would result in more precise estimates, I implement a sharp RD design that represents an ITT analysis. The fixed effects analysis is also on an ITT basis, as the difference between children born before and after the cutoff is eligibility status, not uptake of the program. The fixed effects analysis rests upon assumptions and would be compromised if siblings are treated differently based on birth order, which is likely, or if girl children are systematically treated differently than boy children. The finding of no significant
28
spillover effects is not distinguishable. Insignificance could either be because the three-year apart eligibility rule was strictly enforced or because there were truly no spillover effects. Information about check-ups after three years of age would be necessary to differentiate between these two possible causes. Finally, research on heterogeneous effects for different quintiles and geographical areas would be particularly interesting and useful for further analysis of the program.
29
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Ap p en d ix A: E ↵ ec ts of B J A on h eal th ou tc om es w it h con tr ol s (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) C h ec k -u p s, C h ec k u p s, He igh t for S tu n te d W ei gh t for T et an u s B C G P ol io R ot av ir u s Y el lo w fe ve r 12-24 m o. 0-24 m o. age vac ci n e vac ci n e vac ci n e vac ci n e vac ci n e E li gi b le 0. 805 ⇤⇤⇤ 1. 031 ⇤⇤⇤ -0. 176 ⇤⇤⇤ 0. 063 ⇤⇤⇤ 0. 024 0. 056 ⇤⇤ -0. 006 0. 022 ⇤ 0. 024 0. 014 (0. 120) (0. 318) (0. 055) (0. 024) (0. 054) (0. 025) (0. 009) (0. 013) (0. 028) (0. 028) M ot h er ’s age 0. 023 0. 024 0. 010 ⇤⇤ -0. 001 0. 003 0. 001 ⇤⇤ 0. 000 0. 001 -0. 003 0 .002 at b ir th (0. 015) (0. 024) (0. 004) (0. 002) (0. 004) (0. 002) (0. 001) (0. 001) (0. 002) (0. 002) M ot h er ’s sc h o ol in g 0. 022 0. 053 0. 041 ⇤⇤⇤ -0. 013 ⇤⇤⇤ 0. 005 -0. 005 0. 002 0. 004 ⇤⇤ 0. 000 -0. 004 (0. 022) (0. 042) (0. 007) (0. 003) (0. 007) (0. 003) (0. 002) (0. 002) (0. 005) (0. 005) D is tan ce to n ear es t -0. 010 -0. 056 -0. 010 0. 004 -0. 009 0. 001 -0. 001 ⇤⇤ -0. 002 -0. 001 -0. 009 ⇤⇤ h eal th ce n te r (0. 025) (0. 040) (0. 007) (0. 003) (0. 008) (0. 003) (0. 000) (0. 003) (0. 004) (0. 005) Ar ea (u rb an = 1) -1. 401 ⇤⇤⇤ -1. 653 ⇤⇤⇤ 0. 205 ⇤⇤⇤ -0. 031 0. 080 0. 084 ⇤⇤⇤ -0. 021 -0. 058 ⇤ -0. 205 ⇤⇤⇤ -0. 165 ⇤⇤⇤ (0. 264) (0. 431) (0. 076) (0. 030) (0. 073) (0. 030) (0. 022) (0. 032) (0. 062) (0. 057) T ot al m em b er s -0. 127 ⇤⇤ -0. 282 ⇤⇤⇤ -0. 050 ⇤⇤⇤ 0. 010 0. 005 -0. 004 0. 002 ⇤⇤ -0. 004 0. 004 0. 006 in fam il y (0. 053) (0. 087) (0. 016) (0. 007) (0. 015) (0. 007) (0. 001) (0. 003) (0. 007) (0. 006) C on st an t 5. 638 ⇤⇤⇤ 14. 880 ⇤⇤⇤ 0. 257 ⇤⇤⇤ -1. 564 ⇤⇤⇤ 0. 459 ⇤⇤ 0. 804 ⇤⇤⇤ 0. 974 ⇤⇤⇤ 0. 948 ⇤⇤⇤ 0. 996 ⇤⇤⇤ 0. 911 ⇤⇤⇤ (0. 551) (0. 857) (0. 149) (0. 067) (0. 145) (0. 066) (0. 019) (0. 039) (0. 077) (0. 080) N 1232 1218 1219 1219 1136 1080 383 382 363 371 N o tes : T h is tab le sh ow s th e e↵ ec ts of th e B J A on h eal th ou tc om es u si n g a re gr es si on d is con ti n u it y ap p roac h w it h a b an d w id th of 182 d ay s. He igh t for age an d w ei gh t for h ei gh t ar e re p or te d in z-sc or es of st an d ar d d ev iat ion s an d vac ci n at ion var iab le s an d st u n ti n g ar e re p or te d as d u m m y var iab le s for 1 if re ce iv ed an d 0 if n ot . T h e d at a is fr om th e 2012 E S NUT su rv ey . S tan d ar d er ror s ar e in p ar en th es es . ⇤p< 0 .10, ⇤⇤ p< 0. 05, ⇤⇤⇤ p< 0. 01
Appendix
Ap p en d ix B : E ↵ ec ts of B J A on lon g-te rm h eal th ou tc om es w it h con tr ol s (1) (2) (3) (4) (5) (6) (7) (8) Has re sp ir at or y Has a p h y si cal o r Has h ad d iar rh ea Has p rob le m s Has se ei n g Has h ear in g sp eak in g H as a le ar n in g p rob le m s m en tal d is ab il it y in las t 6 m on th s p h y si cal ly m ov in g p rob le m s p rob le m s sp eak in g d is ab il it y E li gi b le -0. 026 -0. 016 -0. 020 -0. 006 ⇤⇤ -0. 004 0. 002 -0. 004 -0. 006 (0. 065) (0. 017) (0. 049) (0. 003) (0. 0 04) (0. 004) (0. 005) (0. 004) Ar ea (u rb an = 1) -0. 143 0. 039 ⇤ -0. 023 0. 006 -0. 003 -0. 00 6 0. 005 0. 004 (0. 090) (0. 022) (0. 065) (0. 005) (0. 004) (0. 005) (0. 007) (0. 006) P ov er ty le ve l of 0. 067 ⇤ -0. 007 0. 010 -0. 001 -0. 001 0. 001 -0. 002 -0. 001 m u n ic ip al it y (0. 039) (0. 012) (0. 027) (0. 002) (0. 001) (0. 002) (0. 003) (0. 003) M ot h er ’s sc h o ol in g -0. 049 0. 007 -0. 045 0. 002 -0. 001 0. 003 0. 005 0. 003 (0. 041) (0. 013) (0. 030) (0. 003) (0. 0 02) (0. 002) (0. 004) (0. 003) M ot h er ’s age -0. 007 0. 000 -0. 007 ⇤ -0. 000 0. 000 0. 000 -0. 000 -0. 000 at b ir th (0. 005) (0. 001) (0. 004) (0. 000) (0. 000) (0. 000) (0. 000) (0. 000) C on st an t 0. 829 ⇤⇤⇤ 0. 002 0. 455 ⇤⇤⇤ 0. 003 0. 008 -0. 009 -0. 002 0. 010 (0. 192) (0. 038) (0. 147) (0. 004) (0. 0 06) (0. 012) (0. 010) (0. 007) N 222 222 222 1054 1053 1054 1054 1054 N o tes : T h is tab le sh ow s th e e↵ ec ts of th e B J A on lon g te rm h eal th ou tc om es u si n g a re gr es si on d is con ti n u it y ap p roac h w it h a b an d w id th of 182 d ay s. O u tc om e var iab le s ar e re p or te d in d u m m y var iab le s for 0 if n o an d 1 if ye s. T h e d at a is fr om th e 2016 E S D A su rv ey . S tan d ar d er ror s ar e in p ar en th es es . ⇤ p< 0. 10, ⇤⇤ p< 0. 05, ⇤⇤⇤ p< 0 .01
