rafmacalaba/data-use-mentions-extended huggingface dataset:
immobility because of the negative consequences of such shocks on their liquidity. This should come as no surprise: since the determinants of migration, and especially climate-related migration, are complex (IPCC, 2014), it is expected that the sign of the relationship cannot be known _a priori_ , as the direction will depend on local circumstances and is ultimately an empirical question.

# _B. Direct versus indirect effects_

Climate change could exert both direct and indirect effects on migration. In the latter case, one must understand how climatic events affect other drivers of migration, via demographic, socio-economic and political channels. Among the main channels of the indirect effects of weather- and climate-related hazards on migration, the two most important ones are the economic and socio-political drivers. To date, however, there is only limited and partial evidence about these links. Feng, Krueger, and Oppenheimer (2010) provide empirical support about the links between extreme temperatures, crop yields, farmers’ income, and migration from Mexico to the United States. In an important study, Marchiori, Maystadt, and Schumacher (2012) leverage annual panel data from 1960-2010 and find that in Sub-Saharan Africa weather shocks boost rural-urban migration through a decrease in rural wages. In turn, this weatherdriven internal migration into cities brings about downward pressure on urban wages, causing urban workers to move internationally, a mechanism they label the ‘economic geography channel’. Similarly, Dallmann and Millock (2017) find that drought effects on inter-state migration in India are stronger in agricultural states. On top of these microeconomic, household-specific income channels, there is also a macro-level income driver: developing countries are particularly vulnerable to climate-related hazards, because they have a large share of their income in agriculture (the most weather-dependent sector), tend to be hotter and closer to biophysical limits, and lack adaptive capacity to cope with the negative impacts of climate change. For example, using bilateral migration data from 1980 to 2010, Cai et al. (2016) demonstrate that temperature shocks induce international migration
ouster of Taylor. However, row 1 of table 1 reports only three isolated years of civil war, 1990, 1992, and 2003. (Furthermore, all of these years for Liberia are reported as type 3 conflicts despite the involvement of other African countries in the dynamic of this violence; see the next section on the regional question.) 4. This problem of spotty coverage is mitigated by a more lenient coding rule that is presented in row 2 of table 1 based on fewer deaths (PRIO/Uppsala intensities 1–3) and is the mainstay of the MGB studies. However, a new problem appears. There are country-years that are reported as having instances of so-called civil war under the MGB rules but are unknown to us: Burkina Faso (1987), Burundi (1965), Cameroon (1984), Equatorial Guinea (1979), Ethiopia (1960), Gabon (1964), Gambia (1981), Ghana (1966, 1981, and 1983), Guinea (1970), Lesotho (1998), Liberia (1980), Kenya (1982), Nigeria (2004), Somalia (1978), Togo (1986 and 1991), Tunisia (1980), and Uganda (1971, 1972, and 1977). Sixteen of these 22 instances are denoted as “military faction” in the PRIO/Uppsala documentation “Armed Conflicts 1946–2000,” and 17 instances appear in the list of 188 coups by McGowan (2003, appendix A). An 18th, Tunisia, is outside of McGowan’s sub-Saharan database. The data thus seem to report other types of isolated violent episodes. Moreover, anything termed a civil war with a duration of only one year seems suspicious. For example, the violent episode in northern Nigeria that produced the 2004 entry was one of many in Nigeria’s violent post-1970 history. This conflict appears in the data as an intensity 1–3 event (25 or more deaths) and thereby assumes the same civil war status
Growth in either urban sector reduces the rural poverty gap. The ratio of the two proportionate effects on rural wages is: Thus Proposition 1 follows.

So even in this simple model we cannot predict which urban sector will be the most rural-poverty reducing. When city size is small ( _N c_ approaches zero) technical progress in that sector will bring negligible gains to the rural poor via the labor market. Alternatively, even when the city workforce is as large as that in the secondary towns, economic growth in the cities will bring less gain to the rural poor if labor demand is less wage elastic in the cities than the towns. But these are special cases, and one can readily find counter-examples, such as when the city workforce is either relatively large or its labor demand is more wage elastic.

Proposition 1 also suggests that we may well find that town growth tends to matter more to the rural poor at early stages of overall economic development, assuming that this entails that cities expand (in number or size). But in due course, this will change, such that cities become the stronger driver of rural poverty reduction. This is implied by the above model if the wage elasticities of labor demand change little as the share of the workforce living in cities grows, with that in towns falling.

# **III. Data and Descriptive Statistics**

# _3.1 Poverty Data_

Our poverty data are based on estimates of real household consumption that are measured in four “thick” rounds of household surveys conducted by the National Sample Survey Organization (NSSO). These “thick” rounds each have a sample size of over 100,000 households as opposed to the more frequent “thin” rounds. We use data from 1993/94 (50<sup>th</sup> round), 2004/05 (61<sup>st</sup> round), 2009/10 (66<sup>th</sup> round), and 2011/12 (68
the steps for the cleaning of names are as follows:

1. Eliminate from the list of firm names those entries that are not proper names (numbers, addresses, and the expressions ‘NIL’, ‘N/A’, or ‘To the order’).

2. Remove from firm names a list of stop words, geographic stop words, and symbols that are not letters nor numbers. The list of stop words was selected based on text analysis indicating the most common words appearing in firm names, such as ‘corporation’, ‘international’, ‘limited’, and ‘llc’. We also remove prefixes and suffixes (such as ‘co’, ‘sa’, and ‘pvc’) from firm names.

3. Based on the list of pre-processed firm names obtained in Step 2, we use N-gram similarity (using cosine distance metrics) to identify potential pairs of similar firm names (using a lower similarity threshold of 0.6, where 1 means two names are identical).

4. Potential pairs of similar firm names identified in Step 3 go through an algorithm to more precisely determine if they are really similar based on Levenshtein distance (a measure of similarity between two strings). Distance cutoffs defining what is a “small” distance between a pair of names are determined through machine learning algorithms based on subsamples of firm name pairs whose similarity was determined through manual inspection.
21 those who had stopped fuel stacking, perhaps reflecting the ease of cooking with LPG for small families. Figure 13 compares household size for the top two expenditure quintiles in the countries covered in Table 1. The top quintile in Cameroon, Ghana, and urban Kenya had the largest disparity in household size between those abandoning and those stacking polluting fuels. Table 1 shows that households abandoning other fuels in the top quintile in these three countries spent considerably less on LPG in absolute terms than fuel-stacking households, but up to 20 percent more in terms of LPG expenditure shares. Given the LPG expenditure share was only 1 percent in Ghana in the top quintile even for those who had abandoned polluting fuels and yet four-fifths of all households in the same quintile had retained the use of polluting fuels, affordability may not be the main reason for fuel stacking.

**Figure 13  Comparison of sizes of households abandoning versus stacking polluting fuels**

<!-- Start of picture text --> Q4 abandoning<br><!-- End of picture text --> _Source_ : World Bank staff calculations using household survey data. _Note_ : The solid portions are incremental household sizes for those staking fuels. For example, in the top quintile in Cameroon, the average size of households abandoning polluting fuels was 2.1, and that of the households stacking fuels was 3.9. * = urban households only; Q4 = quintile 4; Q5 = quintile 5; abandoning = LPG-using households that had abandoned polluting fuels; stacking = households citing LPG as their primary cooking fuel and were using polluting fuels in parallel.

When household sizes are compared across expenditure quintiles, unsurprisingly it becomes clear that there is no simple pattern with respect to household size. In every one of the 10 countries, the average size of the households with fuel stacking in the top quintile was smaller than that of LPG-consuming households abandoning all other fuels in the fourth quintile. This can be seen by comparing the full height of the green bar in Figure 13
between our indicator of business climate and<sup>the political and financial risks indicators</sup> reported in the preceding section.

**Table 4. Econometric results: sensitivity**<sup>**of business climate to policy variables**</sup>

**(T-statistics in parenthesis)**

||Panel d|ata a|Cross C|ountry|
|---|---|---|---|---|
|Dependant variable|FDI business<br>climate|FDI inflows|FDI business<br>climate|FDI inflows<br>|
|Economic growth|0.123<br>_(1.90)_||0.101<br>(1.71)|0.587<br>_(1.96)_<br>|
|Trade openness|0.163<br>_(2.43)_|2.812<br>(3.23)|0.172<br>_(1.94)_|1.812<br>_(1.50)_<br>|
|Illiteracy rate|-0.209<br>_(-0.39)_|1.097<br>(1.09)|0.139<br>_(1.33)_|0.489<br>_(0.80)_<br>|
|Telephone lines|-0.0404<br>_(-0.51)_|-0.407<br>(-0.42)|0.0129<br>_(0.15)_|-0.144<br>_(-0.46)_<br>|
|Urban population|-0.978<br>_(-1.21)_|-
% of the total benefits. In comparison, costs for the phone-based approach would be negligible.

When it comes to speed, in-person data collection for an asset-based (or PMT) targeting approach typically takes months or years to prepare and implement (World Bank, 2020). The CDR-based approach can be rolled out comparatively quickly — but there are still practical hurdles to implementation. First, training data for the CDR-based poverty prediction model must be collected, preferably shortly prior to program roll-out (Aiken et al., 2021). While in the TUP project training data was collected in-person in a household survey, in other contexts training data collection was expedited via a phone survey (Blumenstock et al., 2015; Aiken et al., 2021). Even if data is collected over the phone, it will typically take several weeks to design a survey instrument and collect data. Second, the CDR-based method requires data from mobile network operators. Data sharing agreements with mobile network operators take at minimum a few weeks to arrange, and substantially longer in the worst case (Milusheva et al., 2021). Third, and finally, training a CDR-based poverty prediction model is expensive in 33
# **5.2 Test-score scaling**

Next, we explore sensitivities to score scales, comparing our results based on scores rescaled via a linear transformation of 300 points to the original HLO score scale. This enables us to use a scale that starts at zero, which has useful statistical properties. In Appendix Figure B2, we corroborate this _de facto_ floor with data from EGRA, which shows that an HLO score of 300 corresponds roughly to zero percent reading comprehension.

Appendix Figure B3 compares the _L_<sup>_h_</sup> _i_<sup>valueusingthetwoscorescales.Whilethescalethat</sup> we use largely does not affect relative ranks, it does affect the degree of the absolute learning adjustment. Using the original scale (y-axis), the distance between Mexico and Ghana is 0.2; by contrast, under the re-scaled version (x-axis), the distance is closer to 0.5. Appendix Figure B4 compares results using the two score scales. In Panel A, we see that the main effect of the rescaling is to reduce the micro-LAYS values that are based on participation impacts—for example, conditional cash transfers in Malawi. This is because under the original scale, the maximum learning adjustment discounted a year of school by about half, since the _de facto_ floor of the HLO scale was 300, which produced a learning-adjustment factor, _L_<sup>_h_</sup> _i_<sup>,of0.48relativetothehigh-performancebenchmark</sup> of 625. Under the rescaling, the minimum learning factor converges to zero, and the learning adjustments drop substantially, reducing participation-based LAYS estimates. As an example, the learning adjustment in Kenya shifts from an original _L_<sup>_h_</sup> _i_<sup>of0.73to0.48,whilecountrieson</sup> the lowest tail of distribution, such as Malawi, shift from a learning-adjustment of 0.57 to 0.18. The re-scaling does not affect the computation of learning-based micro-LAYS, since those values are derived relative
visits and CD4 counts, the data includes all outcomes observed between recruitment into the study and completion of the FEATS experiment. The advantage of the latter approach is that the statistical power of the analysis increases dramatically, because observations included in the analysis originates from patients’ records and is therefore not dependent on a patient interview having been conducted with the said FEATS study participant.) The analysis conducted in this study comprised the following: _Firstly_ , we assess balance at baseline in adherence outcomes and other observable socio-demographic characteristics, by original intent-to-treat status and actual treatment arms (Tables 2-5). On the basis of this evidence, we reflect on the presence of potential selection bias. _Secondly_ , we employ basic bivariate analysis to assess differences in our main outcomes, i.e. self-reported adherence outcome, timeliness of clinic and hospital visits, and immunologic response, across treatment arms for intent-to-treat and actual treatment status (Tables 6-7; Figure 7-8). The statistical significance of differences in means and medians are assessed using t-tests, F-tests and Wilcoxon rank-sum tests. _Finally_ , we employ fixed effects (FE) linear regression models with Instrumental Variables (IV) and random effects (RE) linear regression models adjusted for selection bias to investigate the impact of the FEATS experiments on self-reported adherence, timeliness of clinic and hospital visits, and immunologic response to ARV treatment (Tables 8-10; Figure 9). In each case, we control for basic sociodemographics and ARV treatment duration. Following suggestions by Angrist et al (1996) and Greenland (2000), the original intent-to-treat status is used as instrument to adjust for selection bias in the fixed effects (FE) regression analysis, while in the random effects (RE) regression analysis the inverse Mills ratio is used to adjust for selection bias. To be deemed significant for the purposes of discussion, results need to be statistically significant at least at the 95% level (although results significant at a 90% level are reported).

# **4. Results**

At baseline, age
sample. The set of candidate variables included all area-level remote sensing indicators as well as superarea dummies, although no super-area dummies were selected in Tanzania. In each country, the lasso selected a small number of predictor variables, only 3 in Tanzania and 8 in Sri Lanka. The dependent variable is headcount poverty, expressed as a percentage from zero to one hundred. In Sri Lanka, less annual variability in rainfall as well as a positive rainfall shock in the first quarter are associated with lower poverty rates. In Tanzania, districts with larger buildings are much less poor, as are areas with a larger share of built-up area, while more rural districts tend to be poorer. Despite containing only three variables, the Tanzania model explain half of the variation in non-monetary poverty rates. Meanwhile, the eight Sri Lanka variables explain only 26 percent of the variation in headcount poverty across subdistricts. Overall, the results suggest that the Fay-Herriot estimates, despite using predictors that only vary across area, can significantly improve on the efficiency of the direct estimates, particularly in Tanzania where the model fit is especially good.

_Table 5: GLS coefficients from Fay-Herriot estimation_

|**Sri Lanka**||**Tanzania**||
|---|---|---|---|
|Mean nighttime lights in 2016|-0.003|Mean area of nearest 25 buildings.|-19.45***|
|1990 Built-up area (GHSL)|-0.006|Percent built-up area (Global Urban<br>Footprint)|-2.56*|
|Standard deviation of rainfall|0.006***|Share rural|0.83|
|Rainfall deviation from historical<br>mean, Q1|-12.16***|Constant|84.70***|
|Colombo|-4.55**|||
|Gampaha|-3.80*|||
|Matara|-
employment for these countries.<sup>1</sup> 1 We gauged the accuracy of these data with comparisons to other data sources. For the recent total manufacturing employment numbers reported in the Economic Transformation Database, we looked at estimates of manufacturing employment based on firm-level data sets and Living Standards Measurement Study (LSMS) surveys for Ethiopia and Tanzania. This exercise leads to a reduction in total employment in manufacturing in recent years but no change in the aggregate patterns. A summary of these results can be found in Diao et al. (2021). For the INDSTAT2 employment data, we also plot formal sector employment data in Ethiopia, Tanzania and Vietnam--the three countries for which we have longitudinal census data for the formal manufacturing sector (these data are described extensively in Diao et al. 2021). The INDSTAT2 series and the series of formal sector employment data coincide almost perfectly. This is not surprising since UNIDO obtains its manufacturing employment data from national statistical agencies, but it is nevertheless reassuring.

7
productivity is ambiguous.

There is wide consensus in the published estimates that MNREGA increased unskilled wages by between 5% and 8%, increased labor participation in public works, and may have led to declines in the supply of labor to the private sector (Azam, 2011; Berg et al., 2012; Imbert and Papp, 2015). Imbert and Papp (2015) show that MNREGA increased wages of low-skill workers by 5% on average and this increase is concentrated in the dry season, when they show the bulk of MNREGA work occurs, and is accompanied by a decline in private sector labor supply of 1.3%. When they focus on the states in which the fraction of time spent on public works projects by rural, prime age adults was above 1 percent (“star” states), they find wages increased by 9% and private sector employment fell by 3%. Deininger and Liu (2013) show that MNREGA led to an increase in the accumulation of non-financial assets in the medium run. Raghunathan and Hari (2014) show that farmers plant riskier crops after the implementation of MNREGA which increases their incomes above the direct wage support of the program. Berg et al. (2012) suggests that the wage increase takes between 6 and 11 months after program implementation to materialize and is biased towards low-skill labor.

In the only large-scale RCT on MNREGA to-date (Muralidharan et al., 2016) (MNS) show that improving the implementation of MNREGA increases wages by 7%.<sup>14</sup> They focus only on Andhra Pradesh but note that the similarity in the size of their estimates on the impact of improving MNREGA to the impacts of initial implementation highlight the importance of implementation heterogeneity. They also do not find substantial evidence of impacts on migration but note that their migration data differs from the data used in previous studies.<sup>15</sup> The impact of MNREGA on education also suggests MNREGA tightened local labor markets. Shah and Steinberg (
# **4. OCCUPATIONAL PLACEMENT AND COUNTRY OF ORIGIN ATTRIBUTES**

# **_4.1. EMPIRICAL FRAMEWORK_**

This stage of the analysis is an exploration of the extent to which the predicted Occupational Placement Improvements can be accounted by country-of-origin specific factors. Previous literature focusing on earnings found country attributes to be significant determinants of both the entry wages and their growth rates (Jasso and Rosenzweig, 1986, Borjas, 1987, Borjas 2000). Mattoo et al. (2008) identified two types of country specific influences on the initial levels of occupational placement. First are related to the quality of education in the home country and explain why nominally identical educational qualifications obtained in different countries are valued differently on the US labor market. The second are selection-related and determine which particular segments of the origin country skill distribution are likely to migrate to the US.

As a first step, we check whether the predicted occupational placement indicators for the two sets of hypothetical individuals, migrating in 1975 and 1985 respectively, are influenced by several quality and selection specific attributes. The functional form is presented in equation (3) The regression is estimated separately by hypothetical individual and census year (t=1980, 1990, 2000) for each OP specification (prestige index, education index 1, education index 2). The dependent variables are the levels of performance in 2000 for the 1975 arrivals, and in 1990 for the 1985 arrivals. This means estimating 6 (2 years*3 OP definitions) regressions for the 1975 arrivals, and 3 (1 years*3 OP definitions) for the 1985 arrivals.

The explanatory indicators capture a country’s condition around migration time, i.e. during the 1970s decade or its first half for the 1975 arrival, and during the 1980s, or its first half, for the 1985 arrival. GDPpc stands for log of per capita-GDP in constant 2000 prices averaged over 1970-1975, and 1980-1985 periods, respectively, and is from the Penn World Tables (Version 6.2)
An alternative to the firm closure approach followed by Kong, Meng, and Zhang (2009) is to examine directly the demand for labor among firms. This approach was followed in the China National Firm Survey (CNFS 2009) conducted by the People’s Bank of China in October 2009.<sup>4</sup> The CNFS is a representative sample of over 2,000 manufacturing firms from eight provinces: four coastal provinces (Guangdong, Jiangsu, Shandong, and Zhejiang), one northeast province (Jilin), one central province (Hubei), one northwest province (Shaanxi), and one southwest province (Sichuan). The sampling frame is certainly skewed toward larger and well-established firms: it comprises all firms operating in August 2009 that ever had a credit relationship with any financial institution. Still, it provides interesting evidence of the impact of the financial crisis on the formal sector.

The survey collected data on six-month intervals beginning in 2007, allowing the researcher to examine changes in employment among firms that had survived the financial crisis through October 2009. Table 1 shows the percentage changes in employment over the previous six months. Between January and June 2008, and in the wake of macroeconomic adjustment and implementation of the Labor Contract Law, employment grew by 3 percent. Behind this number, however, was a negative shock to employment in the state and collective sector that was more than offset by continuing increases in employment in other ownership sectors. By December 2008, overall employment in these firms had dropped a half-percentage point **,** but again the average obscures the sharper hit that exporters experienced. Exporting firms shed 1.9 percent of their employees, which implies a reduction in the growth rate of employment of 4.9 percentage points relative to the pre-crisis trend of 3 percent. Ownership sectors—the sector open to foreign investment, of which a significant share goes toward exports to developed economies—shed nearly 5 percent of their employees.

In a comparison of changes in the employment of