rafmacalaba/datause-encoder-data huggingface dataset:
problems for men, chronic gastro-intestinal (CGI) problems (particularly for men), chest pains, wearing glasses (for men) and “other problems” (men and women). Amongst the diseases recorded, the strongest predictors of overall _SAH_ are heart attacks and high blood pressure.

We also tested two extended versions of these regressions. In the first, we included controls for socio-economic variables that could influence the structure of reporting biases in _SAH_ or pick up omitted health attributes. We added controls for household expenditures, personal incomes, education, workforce participation, demographics and regional effects. The results are also given in Table 3. The controls do not add much to the explained variance. However, a number of the controls were highly significant, notably education and the regional effects; we return to discuss these later. We find that the coefficients on the specific health attributes tend to increase when we add the controls. This is most dramatic for the cluster of variables, “had surgery last year” through to “other problems” (Table 3). Adding the controls makes the coefficient on past surgery more negative, and it becomes significant at the 1% level. The controls have a similar effect on the coefficients on “wearing a hearing aid” which only diminishes _SAH_ significantly when the controls are added. By contrast, the coefficients on “feeling chest pain” and wearing glasses (for men) become insignificant when the controls are added. The overall pattern is suggestive of adaptive behavior, whereby people with worse objective health status tend to adapt by overstating their subjective health. Thus the resulting negative correlation between objective health and the error term in the _SAH_ regressions without controls tend to bias downward the regression coefficients.

The second extension added health attributes from 2000 using the panel, to test for lagged effects consistent with adaptation. (Recall that we cannot do this for the physical activity data, which were only asked of pensioners in 2000.) This means a lower sample size, with 2,600 and 17
Census 1990, and met the criteria by which I constructed this paper’s dataset: employed, not living in group quarters, not in school, having entered the US in the 1970s or the 1980s.

The US Censuses are among the richest databases available. However, as I mentioned before, they have caveats. First, it is impossible to follow the exact same individual through several censuses. In addition, censuses do not identify the illegal immigrants and do not track return migration. Finally, throughout decades, there have been changes in methodology and coverage. Thus, the fact that the question asking for the year of immigration was reformulated between the last two censuses complicates the task of accurately isolating immigrants by cohort. The 1980 and 1990 questionnaires require that individuals report the year they came to stay, while the 2000 one asks for the year they came to live in the US, implying that for those having entered the country a multiple number of times, prior experience may pass unobserved. In addition, some individuals may declare the year of immigration as the year when they received their permanent residence, although they may have already spent time in the US as students, on work visas or as illegal migrants.<sup>27</sup> Since censuses are filled out in spring, I assume the information gathered by Census 1990 about immigrants arriving in 1990 cannot fully mirror the degree of comprehensiveness available for that year as of Census 2000, therefore I choose to exclude the 1990 arrivals from the 2000 dataset. The same issue also arises with respect to Censuses 1980 and 1990. For the reasons detailed above I consider interval 1975-1980 reported by Census 1980 equivalent to 1975-1979 reported by Census 1990.

Censuses 1980 and 1990 report years of immigration as intervals, while Census 2000 reports the individual years. For the sake of consistency, I grouped the available data from all three sources into two decades, 1970-1979 and 1980-1989, each with two periods of arrival: 1970-1974 and 1975-1979 for the first; 1980-1984 and 1985-1989 for the second. The periods of arrival proxy time spent on the US labor market. For example, an individual who migrated during 1975-1979 is considered to have spent in the US between 1 and 5 years, counted as of Census 1980.

# **_3.3. EMPIRICAL RESULTS_**

The coefficients based on the estimation of equation (1) with Education Index 1 as a dependent variable are provided in Table 4. Annex table A1 provides the results for the other two

> 27 Jasso et al. (2000) claim that recent immigrants sampled in the decennial censuses “may be neither recent nor immigrant.”

17
Table 5: The growth elasticity of poverty based on GDP per capita

||(1)|(2)|(3)|(4)|
|---|---|---|---|---|
|VARIABLES|||||
|gr_change|-2.263***|-2.464***|-3.148**|-1.264|
||(0.307)|(0.352)|(1.437)|(0.784)|
|initial poverty rate|0.0313|-0.00292|0.0313|0.0426|
||(0.0365)|(0.0405)|(0.0366)|(0.0345)|
|initial inequality|-0.0736|-0.123|-0.130|-0.0988|
||(0.0968)|(0.105)|(0.120)|(0.101)|
|intial GDP per capita|4.04e-06|3.62e-06|4.63e-06|5.31e-06|
||(4.64e-06)|(4.67e-06)|(4.68e-06)|(4.77e-06)|
|Interval|0.00523|0.00302|0.00496|0.00412|
||(0.00366)|(0.00355)|(0.0037)|(0.00379)|
|Baseline: other regions|||||
|SSA||-0.00856|||
|||(0.0297)|||
|gr_change x|||||
|SSA||1.487**|||
|||(0.605)|||
|initial headcount gini|||2.133||
||||(3.107)||
|Baseline: <2000|||||
|2001-2009||||-0.0335|
|||||(0.0286)|
|2010 and above||||-0.0359|
|||||(0.0271)|
|gr_change x|||||
|2001-2009||||-1.273|
|2010 and above||||(0.949)<br>-0.880|
|||||(0.882)|
|Baseline: Consumption|||||
|Income|0.00572|0.00762|0.0048|-0.00448|
||(0.0345)|(0.0374)|(0.0346)|(0.0354)|
|Constant|0.00317|0.0395|0.0281|0.0405|
||(0.0461)|(0.0480)|(0.0591)|(0.0546)|
|country fixed effect|No|No|No|No|
|Observations|574|574|574|574|
|R-squared|0.178|0.186|0.178|0.203|

Notes: Table shows results of a regression of the annualized log change in poverty headcount on the annualized log change in GDP per capita. Sample consists of all consecutive spells between 1981 and 2021, dropping spells with baseline and endline poverty rates lower than 2 percent. Robust standard errors in brackets. ***: Statistically significant at 1%; **: Statistically significant at 5%; *: Statistically significant at 10%.

22
The decision to launch _Red Unidos_ (initially called _Red Juntos_ ), a national umbrella service designed to reduce extreme poverty, was spurred by two key factors. First, the government committed to achieving the Millennium Development Goals (Acción Social 2009). Second, the Colombian Mission for the Eradication of Poverty and Inequality (MERPD) identified a troubling lack of coordination between social agencies that was affecting their effectiveness (World Bank 2013). The MERPD also found incompatibilities in incentives and rules between social programs.

In response, the MERDP suggested adopting a multidimensional strategy, a “social protection system for families in extreme poverty, based on a management model that allows preferential access to public social services” (CONPES 2006). Based on the experience of _Chile Solidario_ , the objective of _Red Unidos_ was to build and strengthen capabilities among extreme poverty and internally displaced families so they can manage their own development to improve their wellbeing and overcome poverty. _Red Unidos_ worked through the following axes (Acción Social 2009):

1. Integrating the public supply of national and local social services according to the demands of the households;

2. Providing family support and advice to households and communities in addition to preferential access, so that the resources and interventions allow poor households to reach minimum living standards; 3. Designing an agreed-upon customized action plan or family framework of coresponsibilities to help households escape poverty.

# **Identification and integration of poor households in** **_Red Unidos_**

Identification of beneficiaries of _Red Unidos_ makes use of the SISBEN, Colombia’s national targeting system based on a proxy means test. The SISBEN has been used to identify vulnerable households through their educational, demographic, and dwelling characteristics. The _Departamento Nacional de Planeación_ (DNP) designs the algorithm, but each municipality collects household information. The resulting SISBEN score ranges from 0 (poorest) to 100 (richest). Each social program identifies its cut-off point to determine eligibility (Departamento Nacional de Planeación 2008).

The implementation of _Red Unidos_ was carried out in three phases. In 2008, the 1.2 million families of _Familias en Acción_ , as well as 300,000 internally displaced families, 19
-11-

Another crucial assumption is that the fee schedule can depend only on variables that both parties can observe. It is assumed that the agent chooses his action before the state of the world is known and that he can observe both the outcome and the state of the world. Hence, different possibilities arise only in respect to information available to the principal. It is always assumed that the principal knows the outcome and that the outcome is a function of the action taken and the state of the world. If the principal can observe actions, for example, he can deduce the state of the world from the action taken and its outcome. This reduces the principal-agent problem to two cases of interest:<sup>3</sup>

# (1) The principal knows the action.

# (2) The principal knows only the outcome.

Case (1) is not a problem of asymmetric information as long as actions can be observed without costs and is, therefore, one of providing incentives given perfect monitoring capabilities. A first best solution to this problem is always found since, in case the agent chooses an inappropriate action, the principal can lower the agent's fee sufficiently to deter such behavior. Fee schedules in this case should be set according to optimal risk sharing with an enforcing constraint that lowers the fee if .y The following section draws heavily on Harris and Raviv (1978), Holmstrom (1979), Shavell (1979) and Rees (1985a).
The measurement of progressivity and redistributive effect thus responds to the concern identified above with the distribution of health care payments, namely that redistributive effect tells us how much more unequal (or equal) health care payments make the distribution of income. This is clearly of interest if our concern is with the level and distribution of income households have available for purchasing food and other "'necessities" after they have paid for their health care. But it does not tell us whether payments are equitably distributed. The second-sub-strand of literature covered in section 3 tries to do this.

# _2.2. Progressivity and redistributive effect of out-of-pocket payments in Vietnam_

Before turning to this strand of literature, we present results on the progressivity and redistributive effect of out-of-pocket payments in Vietnam in the years 1993 and 1998. The data we use are taken from the 1992-93 and 1997-98 Vietnam Living Standards Surveys (VLSS) undertaken jointly by the government of Vietnam and the World Bank. For the purpose of this exercise, the household is taken as the sharing unit for income and payments (both being assumed to be shared equally across household members), but the individual is taken as the unit of analysis. In the case of the 1997-98 survey (which is not nationally representative) the sample is weighted using sampling weights. Household pre-payment income is measured by total household consumption, gross of out-of-pocket payments for health services. Household post-payment income is simply pre-payment income so defined _net_ of out-of-pocket payments. Pre-payment and post-payment income are both defined to be gross of food consumption. Both prepayment and post-payment income are defined on a per capita basis. Out-of-pocket payments are derived in both years from two questions on health spending over the last 12 months, one specifically on inpatient care, the other on all other goods and services associated with the treatment and diagnosis of illness and injury.

Table I shows, for each of the two years, the values of x (pre-payment income), T (out-of-pocket payments), _t_ (the income share of out-of-pocket payments), _Gx_ (the Gini coefficient for pre-payment income), _CT_ (the concentration index for out-of-pocket payments), _7rK_ (the Kakwani index of progressivity of out-of-pocket payments on prepayment income), _CX-T_ (the concentration index for post-payment income vis-a-vis prepayment income), and _ArTS_ (the Reynolds-Smolensky index of redistributive effect for out-of-pocket payments vis-a-vis pre-payment income). It shows that the income share _t_ of out-of-pocket payments fell because income rose faster than out-of-pocket payments. Out-of-pocket payments were regressive on pre-payment income in 1993, but were close to proportional in 1998. Inequality in pre-payment income fell very slightly between 1993 and 1998, but inequality in out-of-pocket payments rose. The degree of _7_
The coverage ratios are for 2000, and are taken from (Demirgüç-Kunt and Sobaci, 2001). We use the inverse of the deposit coverage ratios in our index so as to allow this variable to capture potential _positive_ effects of depositor monitoring, and to be consistent with our treatment of the other sources of monitoring and enforcement, such as rule of law.<sup>7</sup> We also attempt to capture the difference in the _anticipated_ coverage by creating a dummy variable for coinsurance which is found to strengthen the intensity of market monitoring in the literature (e.g., Demirgüç-Kunt and Huizinga, 2004). Coinsurance mechanisms require depositors to bear part of the costs of a banking failure. Our dummy variable equals one if a country has any such arrangement, and zero otherwise.

# <u>E. Other Control Variables</u>

We include the initial level of private credit to GDP (i.e., in 1990) in our regressions to control for the possibility that countries with better developed banking sectors tend to experience slower credit growth. These conditional convergence effects were first made known in the context of cross-country growth regressions, but they have also proved important in financial development regressions.<sup>8</sup> We also include the growth rate of GDP per capita and the inflation rate as macroeconomic controls. Both are averaged over the full sample period. We expect private credit growth to be faster in countries with low inflation and high growth, though inflation and private credit growth might be positively related in an expanding economy. The data on macroeconomic controls are from the World Development Indicators database maintained by the World Bank.

Summary statistics for all variables used in the regressions are in Table 1. Correlation coefficients are reported in Table 2. Neither the correlation between credit growth and related lending nor the correlation between our index of depositor monitoring and related lending is significant. Similarly, the correlations between the related lending index and our control variables are also insignificant, except for the negative correlation with GDP growth. We will

> 7 One potential issue with the construction of Depositor Monitoring is the treatment of countries without explicit deposit insurance.  We assume that the anticipated coverage is not zero and yet small for these countries, and set the value of Depositor Monitoring for those non-deposit insurance countries to the highest value from the countries with explicit insurance (i.e., the lowest coverage limit relative to GDP per capita). However, the implicit insurance can be quite large if government faces a credibility problem without a legally binding coverage limit. In a robustness check, we treat these countries as having the most generous coverage. Our central results turn out to be robust to the treatment of these countries.

> 8 Our results are robust to the exclusion of initial private credit (and other macroeconomic controls). These results are not shown to conserve space.

10
**TABLE 4. ASP SPILLOVERS. EFFECTS ON NONENROLLED STUDENTS.**

||(1)|(2)|(3)|(4)|(5)|
|---|---|---|---|---|---|
|||Gra|des||Behavior|
||Reading|Math|Science|Score|reports<br>(-)|
|[i] Percentage of club participants within|0.007**|0.007***|0.005**|0.007***|-0.011**|
|student’s _n_ classroom (_γ_1)|(0.003)|(0.003)|(0.003)|(0.002)|(0.005)|
|[ii] Spillover efect of adding 3/22 treated<br>students (1 sd)|0.094|0.094|0.080|0.094|-0.147|
|Observations|1357|1358|1357|1356|1194|
|Mean of nonenrolled|6.82|6.58|6.77|6.73|7.33|
|sd of nonenrolled|1.68|1.67|1.70|1.55|1.23|

***, **, * significant at 1%, 5%, and 10%, respectively. Standard errors—clustered at course-by-school level—are in parentheses. Outcome variables are standardized grades at course-by-school level at follow-up. Percentage of club participants was estimated as _Shn_ = ( _Treatedn ÷ Enrolledn_ ) _×_ 100. All regressions include as main control the percentage of enrolled/total students from each course. Individual controls include imputed grades in the course at baseline and a dummy indicating a missing value in the grade at baseline. Average percentage of enrolled/total children per classroom is 13.2% and average percentage of treated/enrolled children per course is 26.5%. Row [i] indicates the coefficients of specification (3) _γ_ 1. Row [ii] indicates the average effect of adding 3 treated students in a classroom of 22 students who enrolled in the ASP (a standard deviation of treated students share _×_ 100 = 13.4%) on nonenrolled academic grades and bad behavior reports. Description of outcome variables is available in Appendix 1.

44
possibilities for intervention and instructional strategies that may help women build both competence and the necessary accompanying self-perceptions of competence.

Finally, more conceptual clarity and precision of measurement is needed to maintain the conceptual integrity of sense of agency across contexts during the adaptation of these measures. In practice, the process of scale adaptation has mostly been approached in an ad-hoc way, for example by picking and choosing items from existing scales that are seen as most appropriate in the local context, as done by Bernard et al. (2014) with the IPC scale. However, beyond more general concerns regarding comparability that arise from an ad-hoc approach, adaptation needs to better account for difficulties in translation and in respondent understanding of the abstract concepts contained in these scales. For example, Frese et al. (2016) find that “entrepreneurship psychology” questions worded in opposite directions produced different factors, most likely due to difficulties respondents encountered in understanding negatively worded questions. A promising approach to deal with this constraint was piloted by Laajaj and Macours (2017) in Kenya, using “beans” as a visual aid for the response scales. In two different reliability tests (test-retest after 3 weeks to measure stability, and Cronbach Alpha calculation to measure internal consistency), this measure of LOC scored second most reliable out of 10 non-cognitive skills the authors measured.

Additionally, personal agency beliefs such as locus of control (contingency beliefs) and selfefficacy (competency beliefs) need to be more clearly distinguished from other psychological or noncognitive measures which do not have as tight a conceptual link to agency. An example comes from Dercon and Singh (2013), who found that girls had lower self-efficacy than boys in India and Ethiopia, and related under-nutrition in early childhood to lower self-efficacy in late childhood/early adolescence. However, their measure of self-efficacy, using the Young Lives survey, combines different psychological measures of control, motivation and self-confidence. Although these kind of psychological measures are related to each other, caution is warranted as policy makers are increasingly designing programs specifically aimed at increasing self-efficacy (e.g., Vasilaky et al., forthcoming). Interventions targeting competency beliefs versus contingency beliefs, for example, will need to be structured differently in order to address different pathways and cognitive levers. In order to build an evidence base that policy makers can draw on in their design of these programs, and in order for researchers to evaluate the effects of these programs, future research should take care to distinguish between sense of agency constructs measured. In a recent review on the adaptation of LOC measures, for example, Huizing et al. (2015) recommend that experts in the understanding and research of locus of control ought to be more involved in the process of validating translated tools in order to ensure that they measure what they claim to measure.

29
countries individuals who dropped out “under duress” from a household shock had worse employment outcomes on average. They were more likely to not be employed (in _nini_ status) or to be employed in the informal sector relative to those who exited school without a household shock. This result supports the hypothesis that household shocks may be driving some students to exit school prematurely and that youth who drop out of school as a result of a household shock accept worse employment opportunities than other dropouts.

It is important to note some of the caveats of our empirical analysis. First, though we put a high effort in accounting for endogeneity, it may continue be an issue in the analysis. In an ideal setting, we would randomize which households receive a negative income shock, and which do not, and then analyze the differences in school drop-out behavior between both types of households. Such experiment is clearly not feasible.

Second, our results are specific to a selected sample. On the one hand, we do not observe the youth who dropped out during middle school (ages 12-15), or before. The sample we analyze is comprised of students enrolled in school, which presumably is a self-selected sample based on unobservable characteristics. The characteristics of such students are probably different from the individuals who already dropped out during middle school (or even elementary school), and that we do not observe in the data. As noted in the analysis, this likely has an impact on the results in the particular case of Mexico where exit rates of younger students are higher. Nonetheless, the analysis of such population is useful for policymaking focusing on building labor forces with more skilled workers. While many steps have been taken to reduce exits at lower levels of schooling, this analysis suggests that more may be needed to protect students in upper secondary and tertiary education as well.

Third, our results are silent about the educational choice of rural students. The surveys we use in our analysis are representative at the urban level only, which limit the scope of our conclusions. While this is a limitation, the reality is that secondary completion rates are often much lower for rural students as are tertiary enrollment rates. Furthermore, the urban population represents the large majority in the three countries analyzed. Again, we still see such conclusions as useful for policymaking analyzing urban settings, where most of the population of the countries we analyze live.

Fourth, our analysis is silent on whether the shock and the exit from school is temporary. Unfortunately, due to data limitations, we cannot observe the same individual for more than four quarters, thus we cannot investigate whether the exit rate is permanent (i.e. can be consider as dropout) or temporary. However, once an individual exits school, the probability of reenrollment is low (for example, Guarcello , Mealli, and Rosati 2003).

25