rafmacalaba/datause-encoder-data huggingface dataset:
**Table 3: Survey Sample and Descriptive Statistics**

|||Baseline||Pa|nel (Round 1|)|
|---|---|---|---|---|---|---|
|Province|HHs|Share w/<br>Migrants|Migrant<br>Pop<br>Share|Panel<br>HHs|Share w/<br>Migrants|Migrant<br>Pop<br>Share|
|Andijan|304|26%|5.7%|115|23%|4.9%|
|Bukhara|358|32%|6.2%|131|25%|4.1%|
|Jizzakh|162|6%|1.5%|59|4%|1.5%|
|Kashkadarya|384|17%|3.8%|147|15%|2.9%|
|Karakalpakstan|440|31%|6.8%|164|30%|6.4%|
|Navoi|201|5%|1.1%|77|1%|0.2%|
|Namangan|320|21%|4.7%|122|19%|3.2%|
|Samarkand|321|25%|5.7%|120|24%|5.0%|
|Syrdarya|100|9%|2.1%|38|18%|3.6%|
|Surkhandarya|203|13%|2.8%|72|15%|3.0%|
|Tashkent|300|4%|1.2%|111|6%|1.1%|
|City of Tashkent|281|2%|0.5%|106|4%|0.8%|
|Fergana|359|21%|4.5%|135|15%|2.6%|
|Khorezm|280|40%|9.5%|106|36%|7.5%|
|Total|4013|19%|4.2%|1503|18%|3.5%|

After completion of the face-to-face baseline, interviewers began regularly calling a randomly selected panel of 1,503 households over the phone to conduct short interviews, following a set monthly schedule agreed to by the participating household. The questionnaire for these phone interviews was designed to monitor trends in migration, subjective well-being, measures of income, employment, service disruptions, and related indicators. Phone-based interviews began on September 5, 2018, and the first eight rounds of the survey are used in the analysis that follows, covering the entire period to the end of April 2019. A total of 12,137 unique observations are available for analysis.

Attrition is one potential concern using panel data of this type. To ensure that non-take-up in the first round (and attrition in subsequent rounds) did not seriously affect the required sample size for survey representativeness, households that refused to participate were replaced with other households drawn from the same sample cluster. However, any systematic difference in the household characteristics due to refusal to participate could lead to bias if the replacement households were different on average (with respect to observable characteristics) from the households that refused. Among the random sample of 1,503 households originally drawn from the baseline, about 25% refused to participate in the first round (i.e. initial take-up in the first phone round totaled 1,122 randomly sampled households, and 381 randomly selected replacement households to make up for those that refused or could not be contacted). Comparing those who agreed and those who refused to participate shows that in general, relevant household characteristics such as total household consumption, migration status, and household size do not differ significantly between the two groups. The exception is that rural households are substantially less likely to drop out of the sample and require replacement. However, random selection of replacements from the same PSU results in near perfect balance when comparing to baseline summary statistics.

7
Christina, Vakis, Renos (2015). ”Wealth Gradients in Early Childhood Cognitive Development in Five Latin American Countries.”, _Journal of Human Resources_ , 49(3), 663-394.

- [24] Tirole, J. (1988). ”The Theory of Industrial Organization”, MIT Press.

- [25] UNESCO (2008). ”The six goals: How far have we come?” Chapter 2 in Education for All Global Monitoring Report, Paris.

- [26] World Bank (2004). ”Inequality and economic development in Brazil.” A World Bank country study, World Bank, Washington DC.

30
# **The Aftermath of Civil War**

## **I.  Introduction**

War has devastating consequences for a country, including death, displacement of people, and destruction of public infrastructure as well as physical and social capital. World Bank (2003), one of the most recent and comprehensive reports, concludes that the economic and social costs of civil wars are not only deep but also persistent, even for years after the end of the conflict. However, when the end of war represents the beginning of lasting peace, there are good reasons to believe that recovery, albeit gradual, is possible. This is what neoclassical models of economic growth and convergence would predict and what the evidence of recovery in Europe (after World War II), Korea, and Vietnam, among others, would seem to indicate. The objective of this paper is to contribute some stylized facts on the evidence regarding the economic, social, and political aftermath of civil wars.

The scarce literature that studies the consequences of civil wars has usually focused on the costs _during_ conflict. Very few studies analyze the costs of civil war after peace agreements are signed; and if they do, they usually concentrate on health-related issues (see Ghobarah, Huth and Russet 2003). Using a cross-section of countries with well defined pre- and post-war periods, this paper gives a general evaluation of the aftermath of internal wars along basic economic, social, and political dimensions. Although this paper is mainly descriptive, it provides some motivation and evidence on various hypotheses surrounding the consequences of internal wars. It will hopefully induce more specific and analytical research in future work.

_Brief review of the literature._ There is little controversy on the dire effects of civil and international wars. They kill people, destroy infrastructure, weaken institutions, and erode social trust. Moreover, the destruction of infrastructure and institutions leaves the population under conditions that increase the risk of disease, crime, political instability, and further conflict. Collier et al. (2003) provide a review of the literature on the costs of civil war. For example, Collier (1999) finds that during civil war countries 2
Under the null hypothesis that the observed persistence is due solely to genetics, the economic mechanisms identified in the theory are unlikely to provide a coherent explanation of the pattern of mobility across countries. We use household income data from Chinese Household Income Project (CHIP 2002, CHIP 1995) and National Sample Survey (NSS 1993) of India to explore the mechanisms behind the pattern of relative mobility (the IGRCs) across farm and nonfarm households. The evidence suggests an important role for the economic forces (returns to education and occupational persistence) in explaining the pattern of educational persistence across farm and nonfarm households, both in rural India and rural China. The theory also suggests that we should observe changes in the intergenerational educational persistence in rural China for the younger generation because of the effects of reform on the relevant mechanisms such as higher returns to education in nonfarm occupations. In contrast to the separability observed for the older cohorts, we indeed find evidence of emerging complementarity between father’s education and nonfarm occupation in rural China for the educational attainment of the younger generation (18-28 years old in 2010).

The rest of the paper is organized as follows. Section 2 develops a model of intergenerational persistence with credit constraint that incorporates the salient features of farm vs. nonfarm households relevant for educational attainment. The next section describes the estimating equations derived from the theory and the empirical issues in understanding potential complementarity between parent’s education and nonfarm occupation in determining children’s schooling. Section 4 discusses the data and section 5 reports the main empirical estimates. The following section explores the evidence on the mechanisms identified by the theory underlying the observed pattern of slope (IGRC) and intercept estimates for the cohorts who went to school in the 1990s or earlier. Section 7 provides evidence on possible changes in the pattern of educational mobility in rural China for the younger generation (18-28 years old in 2010). The paper concludes with a summary of the main results from the theoretical and empirical analysis.

# **(2) A theory of Intergenerational Educational Persistence in a Dualistic Rural Economy**

We develop an extension of the Becker-Tomes model with credit constraint (Becker and Tomes (1986)) to understand the role played by nonfarm occupations of parents in intergenerational educational mobility of children in a rural economy. The differences in expected returns to education in farm vs. nonfarm households are expected to play an 5
where _u j_ =error from the third stage, ε _j_ =error from the first stage, φ _j_ =error from the second stage, σ _j_ =standard error from the unconditioned land value regression,

> <sup>=correlation between the choice error and the land value regression error.</sup>

> <sup>_r_</sup> _j_

Because of selection bias, it is possible that the unobserved profitability of a choice is correlated with the selection of that choice (Heckman 1979). Since the farmer maximizes net revenue conditional on the choice of farm type, the error in the land value equation may be correlated with the errors in the choice equations. According to Dubin and McFadden (1984), with the assumption of the following linearity condition:<sup>2</sup> The conditional profit functions can be consistently estimated as:

> 2 See Bourguignon et al. (2004) for the details of the selection bias corrections from the multinomial choice. They find that Dubin and McFadden’s method is preferable to the most commonly used Lee method, as well as to the Dhal’s semi-parametric method in most cases. Monte Carlo experiments also showed that selection bias correction based on the multinomial logit model can provide fairly good correction for the outcome equation even when the IIA hypothesis is violated.

7
<!-- Start of picture text --> Geological vulnerability Distance to medium sized market (m) Sanitation risk Proportion with piped water<br>ny52z' Pa , ER FicSeeoy263as 0.300.25. 15000 ‘ 0.605 0806<br>o& C3 if Dag?oe a 0. 0.101520 500010000 gf _ o30201 0402<br>0<br>2<br>2<br>Proporton with unimproved water Poverty Private borehole density Water burst density<br>5<br>x‘ 0.20 0.15 0.6<br>2 5 0.15 0.08 0.10 Oa<br>° 0.10 0.06 0s 0.3<br>gz 0.05 0.04 . 54<br>' 0.02 0.00 0.0<br>2<br>2<br>Sewer burst density Distance to water network (decimal degrees) Distance to sewer network (decimal degrees)<br>xr’‘r rde 0.07 om 4 0.10<br>52 18 wet 2 0.050.06 y 0.08<br>o7 1.0 - - Ph 0.040.03 >. 0.060.04<br>2 0.5 0.02 7 0.02<br>*°0.0 >0:00 ~~ # 0.00<br>2<br>30.8 30.9 31.0 31.1 31.2 31.3 314 30.8 30.9 31.0 31.1 31.2 31.3 314 30.8 30.9 31.0 31.1 31.2 31.3 314<br><!-- End of picture text -->
San Cristobal and 2,857 from Suba received one of the treatments. This left 4,072 control students in San Cristobal and 3,505 in Suba, and the students are evenly distributed within gradegender categories.

# **C. Data**

The richness of the available data is one of the major strengths of our study. The data come from six sources. These include general survey data on all eligible families, data collected specifically for the study, and administrative data collected by the SED.

First, we have the data from the original SISBEN surveys from 2003 and 2004 that contain information on all families eligible to register for the lottery. These surveys were conducted as part of the SISBEN national poverty index – in fact, these are subsets of the actual surveys that were used to create the index itself. We have access to all individuals placed into the bottom two SISBEN categories, providing a rich baseline description of all of the eligible families. It also allows us to verify the representativeness of our results by checking that those families who registered for the study were not significantly different from those that did not register. The SISBEN data provide us with several variables at the family level such as schooling level of the household head, physical characteristics of the dwelling, employment status of adults, and family income. It also provides us with individual level variables such as enrollment status at the time of the survey, age, income, and marriage status.<sup>9</sup> The second source of data comes from the program registration process itself. During this process families had to provide some basic information on the students to ensure eligibility. These data include birth date, gender, last grade completed and year in which that grade was completed. Most of this information was verified through the actual SISBEN database and when possible, the SED’s official records.

After the randomization, it became clear that students were spread across a large number of schools, but the density was heavily skewed with the majority of students in a smaller number

> 9 The obvious challenge of using this data is that families knew that they were being surveyed for the purpose of scoring them on a poverty index.  As result, measures of assets and income are probably underestimates of the true values.  However, this bias is almost certainly not correlated with the differences investigated in this paper given the timing and purpose of the survey.  We use this information for two primary purposes.  First we use it to compare registrants to non-registrants, and second we use it as a source of information on the households to which the children in the study belong.

- 12 -
Policy Research Working Paper 7458

# **Abstract**

This study analyzes the extent of downward bias in the calculation of inequality of opportunity for continuous outcomes such as income. A typically recognized source of bias is the unobserved circumstances as there is a limited set of variables available in household and labor force surveys. Another previously overlooked source is the likely unobservable nature of top incomes. Using Monte Carlo simulations where the underlying inequality of opportunity is predetermined at various levels, the study presents three key findings. First, the omission of a relevant circumstance can bias the inequality of opportunity estimate by as much as 80 percent, depending on how much variation of the outcome such

- circumstance explains. Second, not observing the top 5 per cent of the income distribution can lead to downward biases of anywhere between 12 and 35 percent, and the combination of missing the most favored population and even one relevant circumstance exacerbates the bias of the empirical estimates. The third key result is that the estimated inequality of opportunity is strongly correlated with the amount of variation in the outcome variable explained by the combination of circumstances (measured by the R2). This result suggests that in empirical applications, the inequality of opportunity estimate can be roughly (and quickly) approximated using simple econometric techniques.

This paper is a product of the Poverty Global Practice Group. 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://econ.worldbank.org. The authors may be contacted at glaraibarra@ 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
SYS-REVIEW/HI-LMIC In the case of Ghana, Mensah, Oppong and Schmidt (2010) report a higher utilization rate for pregnancy care among the insured, although the sample is small. For Nicaragua (Thornton and Field 2010) and Georgia (Bauhoff et al _._ 2010), insurance targeted mostly to the poor did not induce higher utilization, although the study in Georgia reported higher utilization by those with higher assets. In Burkina Faso (Gnawali et al. 2009) and India (Aggarwal 2010), the two community-managed schemes, there were overall increases in health care use, but there was no impact on inpatient utilization.

Trujillo, Portillo and Vernon (2005) and Miller, Pinto and Vera-Hernandez (2009) indicate positive effects for the same insurance program in Colombia at different times. The insured received care more often, and the latter study reported a higher use of preventive care after changes to the payment structure for the provider. Both studies report no difference in inpatient care for insured and noninsured groups.

For Mexico’s _Seguro Popular_ (SP), studies report differing results: King et al _._ (2009) report no higher utilization for the insured for all health care, whereas Sosa-Rubi, Galarraga and LopezRiduaura (2009) report that diabetics insured under SP have better access to diabetic care compared to the corresponding figures for diabetics who are uninsured.

Three studies of VHCFP from Vietnam report conflicting results. Wagstaff (2007) reported higher utilization rates for inpatient and outpatient care, with substantially higher inpatient care. Axelson et al _._ (2009) reported a small increase in overall utilization, mostly because of increased outpatient care. Although both papers use propensity score matching, they use different data. A subsequent study by Wagstaff (2010), which used a different data and 17
# **Table 3. Panel B - Terms on Loans to the Energy Sector**

This panel displays the impact of bank exposure to the energy sector and its lending to energy borrowers. The dependent variables are _Interest Ratef,b,m_ , which is the total interest rate charged to firm _f_ by bank _b in_ month _m_ ; _Collateralf,b,m_ , which is the fraction of loans that is guaranteed; and _Maturityf,b,m_ , which is the average length in log months of loan duration _. ExposureEnergyb,Aug14_ represents lending to the energy sector as a share of its tier 1 capital of bank _b_ in August 2014 _. Postm_ is an indicator that the month _m_ is after the energy price shock in August 2014. Standard errors double clustered at the bank and month levels. Detailed variable definitions are provided in Table A1. Observations are at the firm-bank-month level for January 2013 to June 2016. *** p<0.01, ** <u>p<0.05, * p<0.1.</u>

||Interest<br>(1)|Ratef,b,m<br>(2)|Collat<br>(3)|eralf,b,m<br>(4)|Matu<br>(5)|rityf,b,m<br>(6)|
|---|---|---|---|---|---|---|
|ExposureEnergyb,Aug14*Postm|-0.13**|-0.11***|0.38|0.51|-0.01|0.03|
||(0.05)|(0.04)|(0.77)|(0.55)|(0.02)|(0.02)|
|Observations|32,358|16,698|32,358|16,698|32,358|16,698|
|R-squared|0.29|0.75|0.81|0.89|0.67|0.83|
|Bank-firm FE|Yes|Yes|Yes|Yes|Yes|Yes|
|Month FE|Yes|-|Yes|-|Yes|-|
|Firm-month FE|No|Yes|No|Yes|No|Yes|
|SD(ExposureEnergyb,Aug14)|6.1|6.1|6.1|6.1|6.1|6.1|

30
The short-term effects showed that the ban reduced work incidence in paid work activities by 4.1 p.p. or 27 percent. It seems the ban reduced the proportion of boys doing paid work and studying and increased the proportion of boys only studying. We found that these effects lasted for five years, from 1999 to 2003 when boys hindered from entering the formal labor force at age 14 reached age 18.

We pooled the PNADs of 2007 to 2014 to estimate the long-term effects of the ban on educational attainment and labor-market outcomes when the cohorts were age 22 to 29. Our pooled effect estimates suggest the ban did not affect those average outcomes among the entire affected cohort in the long term. It thus seems that the higher proportion of boys only studying just counterbalanced the lower level of accumulated labor-market experience. However, it seems to have detrimental effects on a sub-group of the affected cohort that will likely have lower earnings when adults.

It is important to contextualize the findings of this paper. First, we estimated ITT effects, that is, the average effect of the child-labor ban on the entire cohort of boys who turned age 14 in 1999. Since the child-labor ban affected a small share of affected boys (4 p.p.), the ITT estimate captures the lower bound of a local average treatment effect (LATE), that is, the effect on those who dropped out of the labor force at ages 14 or 15 because of the ban.

Second, although we are confident of the internal validity of our results, one should be cautious to extrapolate to different age groups or cohorts. This cohort faced a particular set of constraints and policies that are not the same faced by other cohorts.

One should not read it as an implicit advocacy towards child labor but as a cautionary note that the law should be designed according to the context and compensatory policies—such as a conditional cash-transfer program and/or an apprenticeship program—should be put in place; otherwise it would make individuals worse off by reducing their choice-set.<sup>35</sup> In this regard, our results are in line with a broader literature (for example, Lavy 2015b, Doepke and Zilibotti 2005) that shows that interventions that increase the choice-set and opportunities of children are important policies to help them to achieve their intentional goals.

> 35 The Brazilian conditional cash-transfer program was created in 1996 as a pilot but expanded only in 2001. The Brazilian apprenticeship program was institutionalized only in December 2000.

27
**Table 6. The Effect of PMT on Height-for-Age of Children 6-60 Months: Using Binary Indicator for Program Exposure**

||Pooled<br>|OLS<br>|Commun<br>Effe<br>|ity Fixed-<br>cts<br>|
|---|---|---|---|---|
||(1)|(2)|(3)|(4)|
|**_A. 6-12 Months_**|||||
|Year Dummy (2000=1)|-0.255|-0.345|-0.418|-0.524|
||(0.392)|(0.394)|(0.702)|(0.705)|
|Program Exposure (Yes=1)*Year|0.264|0.384|0.507|0.617|
||(0.383)|(0.386)|(0.712)|(0.722)|
|Time Varying Community Characteristics|No|Yes|No|Yes|
|R-squared|0.14|0.16|0.57|0.58|
|**_B. 12-24 Months_**|||||
|Year Dummy (2000=1)|0.001|-0.035|0.109|0.121|
||(0.231)|(0.235)|(0.241)|(0.257)|
|Program Exposure (Yes=1)*Year|-0.106|-0.063|-0.096|-0.089|
||(0.225)|(0.231)|(0.265)|(0.280)|
|Time Varying Community Characteristics|No|Yes|No|Yes|
|R-squared|0.08|0.08|0.40|0.40|
|**_C. 24-60 months_**|||||
|Year Dummy (2000=1)|0.012|0.042|0.071|0.086|
||(0.136)|(0.137)|(0.187)|(0.187)|
|Program Exposure (Yes=1)*Year|-0.100|-0.125|-0.120|-0.139|
||(0.133)|(0.134)|(0.191)|(0.192)|
|Time Varying Community Characteristics|No|Yes|No|Yes|
|R-squared|0.15|0.15|0.26|0.26|

Note: The dependent variable is the child height for age z-score, and the program effect is a dummy for whether the community had a supplemental feeding program interacted with a dummy for year=2000. Other covariates (with coefficients reported in Appendix Tables A6.1, A6.2 and A6.3) include: gender (boy=1), age (months), father and mother’s education and height, male head of household, farm household, household access to private toilet, sanitation and free health services, distance of village to bus station, community’s access to sewerage and piped water, number of village midwives, presence of a _posyandu_ in the community, and an indicator for whether the community is urban. Robust standard errors are in parentheses. (*), (**) and (***) indicate significance respectively at 10%, 5% and 1%.

32