rafmacalaba/datause-encoder-data huggingface dataset:
Policy Research Working Paper 11067

# **Abstract**

Viet Nam is widely regarded as a success story for its impressive economic growth and poverty reduction in the last few decades. Yet, recent evidence indicates that the country’s economic growth has not been uniform. Compiling and analyzing new, extensive province-level data from the Vietnam Household Living Standards Surveys spanning 2002 to 2020 and other data sources, this paper finds within-province inequality to be much larger than between-province inequality. Furthermore, this inequality gap has been rising over time. Despite the country’s fast poverty reduction, the poor were increasingly segregated in certain provinces, particularly those with a larger ethnic minority population. The analysis finds a beneficial impact of economic growth on poverty reduction, but this can depend on inequality levels. It also finds that greater inequality has had negative effects on economic growth but varying negative effects on different poverty indicators. The paper provides supportive evidence of the beneficial impact of economic transitions from agriculture to non-agriculture. The results suggest that policy makers in Viet Nam should focus on reducing spatial disparities and income inequality to attain sustainable economic development.

This paper is a product of the Development Data Group, Development Economics and the Poverty and Equity Global Department. It is part of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy discussions around the world. Policy Research Working Papers are also posted on the Web at http:// www.worldbank.org/prwp. The authors may be contacted at hdang@worldbank.org and vietcuong@vnu.edu.vn.

_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
# _CHAPTER 7. SEMI-PARAMETRIC AND MACHINE-LEARNING METHODS_ 58

in off-census years, as they are not based on census data. However, they seem to be all synthetic, similar to the traditional ELL method, in the sense of not accounting for area effects. If that is the case, their performance in an application is going to depend on the ability of the auxiliary information at hand to explain the between-area heterogeneity of the variable of interest. They might achieve great efficiency gains in an application where the covariates fully explain the between-area heterogeneity, but result in very poor estimates when the covariates are week in that sense. Note that to evaluate small area estimators, we need to look at their true MSE (accounting for both, bias and variance), since the produced MSE estimates might be biased low, giving a misleading picture of the true efficiency of the estimators. In real applications as those reviewed above, true MSEs are not available. The only way of having the true MSE is conducting simulation experiments.

Corral, Henderson and Segovia (2023) conducted design-based simulations based on a real census that included an income variable, by drawing multiple samples from it. They showed that, in the case of weak auxiliary information, such as the geo-referenced area-level data in their study, gradient boosting techniques applied at the area or cluster (PSU) level perform very poorly compared to other SAE procedures, both in terms of design bias and MSE. However, when using much more powerful census auxiliary area-level information, the same technique performs well in terms of design bias and MSE, close to the gold standard EB method based on the richer unit-level census data and including area effects. The EB method has a more consistent performance in terms of design bias and MSE than the machine learning procedures, even when the auxiliary information is week. Hence, their results point out the need to include area effects in modern machine learning procedures as well.

Moreover, the methods for aggregated data in certain locations that use survey estimates as a response variable in the models do not take into account the sampling errors of these survey estimates. These sampling
province to identify the eligible population. This exercise started with a wealth ranking in 100 villages performed by CHA in partnership with village leaders, yielding a population of 26,957 households that were split into four community-defined categories: well-off (6%), better-off (16%), poor (34%), and ultra-poor (44%). This was followed by a verification survey, administered by CHA, to measure the six qualifying criteria for being eligible for the TUP program listed above. This removed 85% of the households identified as UP from the wealth ranking exercise. MISFA then completed a final verification exercise, removing 28% of this group whose initial eligibility was overturned due to reporting inconsistencies. This resulted in an eligible group of 1,235 households, or slightly under 5% of the population in our study area.

A baseline survey was conducted among all eligible households from February to April 2016, before a public lottery to identify TUP participants took place in May 2016. The randomization was stratified by PRA group by holding separate lotteries for each. Most villages (51) had one PRA group, while larger villages were split into multiple PRA groups which were typically defined by the feeder area of a masjid (mosque). PRA groups with one TUP-eligible household were removed from the study due to the infeasibility of a lottery in these cases, effectively dropping 16 study households from 16 PRA groups. This resulted in 133 PRA groups and subsequent lotteries across our study sample. Then 1,219 UP households in 80 villages were randomly assigned into one treatment group (491 households) and one control group (728 households). Starting in May 2016, the treatment group received the full TUP package as described above, and the control group did not receive any of the components. The program lasted for 12 months from the time of asset transfer. A follow-up survey was conducted from July to October 2018, approximately 1 year after program completion and 2 years after the asset transfer. In this study, we present estimates of the impact of the program on UP households, comparing the treatment and control groups at the first follow-up. Figure 4 provides a graphical representation of how the final study sample was generated.<sup>13</sup>

> 13 To avoid the potential for data mining generating spurious relationships, we registered the trial in the American Economic Association Randomized Controlled Trial registry and prepared a pre-analysis plan, pre-specifying all primary and secondary outcomes and measurement approaches: <u>https://www.socialscienceregistry.org/trials/2665. All de-</u> identified data will be made available on the World Bank’s Microdata Catalog and coding files used to generate the results in this report will be available on GitHub. The study also has the Institutional Review Board (IRB) clearance from Princeton University and the Ministry of Public Health in Afghanistan.

13
checks, and a final section concludes with some thoughts on policy implications.

# **2 Data and Methodology**

## **2.1 Description of the Data**

Our dataset comprises an unbalanced panel of 77 developing and developed economies over the period 1976–2005. The variables included in the data set are described in Appendix Table A.3, and the full set of countries for which data on all our variables of interest are available for at least one 5-year period is presented in Appendix Table A.5 (along with the average index values for selected key variables for the last five-year period). We compute five-year period averages (standard deviations in the case of volatility measures) for all the variables listed in Table A.3.<sup>7</sup> We do so for two main reasons. First, the measures of export diversification that we employ are potentially subject to noise that is not necessarily reflective of a true diversification trend in the export basket. Other control variables such as the per capita growth rate may be subject to business cycle variations. Five-year averaging serves as a filter that would remove noise and mute cyclical elements in the data. Second, the econometric tool we employ as our benchmark (system GMM) was designed to work with data that include a large cross sectional and a short time series dimension. Taking 5-year averages yields a maximum of 6 time periods for any given country, which would then satisfy this short time-series requirement.

Due to the large number of variables included in the dataset, we limit our discussion here to the key dependent and independent variables, leaving details of the construction of other variables to the technical appendix. Our main dependent variable is output growth volatility, measured as the standard deviation of GDP per capita across each 5-year period. While it is entirely plausible to substitute _output_ for growth volatility, we refrain from doing so for three main reasons. First, even a stable growth path at a constant annual rate of growth will generate a positive volatility measure, even though this is both a desirable and perfectly forecastable outcome. Second, policymakers are generally more concerned with maintaining a stable growth rate, as opposed to stable output levels, since it is the former that directly affects the planning horizon. Third, we

> 7It can be argued that using non-normalized standard deviations as measures of volatility risks overstating volatility for countries with high growth rates relative to those with low growth rates. We refrain from normalizing standard deviations for several reasons. First, the issue is likely to be less of a problem in a dynamic panel setting such as in this paper. Second, in practice the differences in standard deviations of growth typically turn out not to be driven by differences in mean levels of growth. Third, normalizing by the average may lead to large outliers when the average growth rate is close to zero.

7
<!-- Start of picture text --> Figure 1:<br>EMIGRATION TO THE EAST AND WEST AND CHANGE IN COMMUNIST PARTY<br>VOTE SHARES BETWEEN 2005 AND 2009, BY DISTRICT<br>(based on census data and official election results)<br>0 .02 .04 .06 .08<br>prevalence of migration to russia 2004<br>0 .02 .04 .06 .08<br>prevalence of migration to western europe 2004<br>.3<br>.2<br>.1<br>0<br>change in communist votes' shares 2005-2009 -.1<br>.3<br>.2<br>.1<br>0<br>change in communist votes' shares 2005-2009 -.1<br><!-- End of picture text --> as well as return migrants signi...cantly increase participation rates, and more so for the latter. Interestingly, in the spirit of Spilimbergo’s ...ndings, they ...nd that only migrants to the US seem to make an impact, while migrants to Portugal, the other main destination, do not. In contrast, they do not ...nd evidence of additional e¤ects for skilled migrants. The other context is that of Moldova, a former Soviet Republic with virtually no emigration before 1990 and which has seen a recent surge in migration out‡ows, estimated at half-a-million for a population of 3.6 million in 2008. The evidence we present for Moldova, which is purely descriptive, comes from the analysis of election outcomes in 2005 and 2009 (Omar Mahmoud et al., 2010). It shows that higher votes for the communist party are associated at the district level with migration to Russia while a negative correlation obtains for migration to the EU. Moreover, changes in the share of votes gained by the communist party between 2005 and 2009 follow the same pattern (see Figure 1) and there is evidence of spillover e¤ects to non-migrant households as the same voting patterns are observed even after excluding households with a (current or past) migrant member.

At a macro level, the only paper attempting to assess the overall e¤ect of emigration on institutions we are aware of is Li and McHale (2009), who use the World Bank 5
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randomly selected households had completed their latrines and that 90% (144/160) of the latrines were in use (the study provided no information about toilet coverage before and after the campaign) [20]. Taken together, these studies suggest that sanitation behavior change interventions result in toilet construction, but fall short of achieving “total” sanitation (or, 100% open defecation free communities). Two recent working papers that study India’s TSC have attributed large improvements in child height-for-age to the TSC. However, one study used administrative monitoring data collected by the project implementation teams which has been discredited due to vast over reporting compared to data from the recent census [43]. The second study from Maharashstra is a cluster-randomized trial [49]. While the study design is robust and the findings are important, the effects on height-for-age seem too large given the study included many children beyond the age of growth faltering (24 months) and only 8 percentage points in toilet construction [see 50]. Furthermore, there are no results published in peer reviewed journals on the health effects of TSC-style programs even though improved health has been a central benefit used to motivate the elimination of open defecation [22].

# **2.  Background and Description of the Program**

The government of India launched the Total Sanitation Campaign (TSC) in 1999, and at the time of this evaluation it was one of the largest rural development programs in India. The TSC included subsidies for and promotion of individual household latrines, school sanitation and hygiene education, Anganwadi<sup>9</sup> toilets, and community sanitation complexes. The TSC also supported rural sanitary marts and production centers. The TSC included several unique features that distinguished it from earlier approaches to rural sanitation in India, including:

- A campaign-mode implementation approach

- A focus on demand generation through behavior change and communication campaigns

- A shift from high subsidy to low subsidy regimes

- A flexible menu of technology options

- An award, called the _Nirmal Gram Puraskar_ (NGP), which is awarded to communities who are Open Defecation Free (ODF), defined as 100% of the population with access to a private- or shared toilet, and that meet all of the other total sanitation requirements. The award includes money and formal recognition to help incentivize entire communities.

TSC funding and program implementation was managed at the district level<sup>10</sup> and program activities were implemented at the community ( _Gram Panchayat_ ) level. Within each district,

> 9 _Anganwadi_ – courtyard shelter in Hindi – is a child-care and mother-care center that is sponsored by the Indian government under integrated child development scheme (ICDS) program. These centers focus on children aged 0-6 years.

> 10 Indian administrative set up consists of central government, then state government, then districts, then blocks, then gram panchayats (GPs).  Each GP consists of one or more villages.  Within each village there can be one or more habitations or neighborhoods.

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# **I.   Introduction**

Recent research in law and finance has examined the legal determinants of external finance. LaPorta et al. (1997) find that legal rules and origin are important in determining the size of a country’s capital markets, especially its equity market. However, the role of legal factors in determining the size of debt markets is less clear. Using firm-level data LaPorta et al. find that the similarity of the ratio of _total debt to sales_ across countries of different legal origins is “... remarkable, and suggests ... a potentially important conclusion: large publicly traded firms get external debt finance in almost all countries, regardless of legal rules” (p. 1148). They conjecture that state intervention in the banking system may be the reason for the similarities.

Other research has examined legal determinants of firms’ capital structure decisions. For example, Demirguc-Kunt and Maksimovic (1999) study _debt-to-capital_ ratios for publicly traded firms in 30 countries and find “that reliance on long-term debt by large firms is clearly higher in countries with an effective legal system” (p. 325), but they also find “no evidence that the index of creditor rights helps predict either short-term or long-term leverage or debt maturity” (p. 329).<sup>1</sup> In addition, Demirguc-Kunt and Maksimovic find that in countries without the right of secured creditors to be paid first in bankruptcy, firms use relatively _more_ short-term debt—evidence consistent with the monitoring hypothesis of Diamond (1991). Similarly, Giannetti (2003) finds that firms in countries with stronger creditor rights have higher long-term debt. Recent work by Fan, Titman, and Twite (2003) examines leverage and maturity across 47 countries finding that a common law system is unrelated to leverage, but that weak legal system integrity, as measured by the corruption level, is associated with high leverage and more short-term debt. In sum, while there seems to be some evidence positively linking _long-term_ debt and legal effectiveness, the role of legal factors in determining the size of total corporate debt is complex and still not fully understood.

> 1 Specifically, they find that creditor rights are unimportant after controlling for legal origins and legal enforcement.

1
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