rafmacalaba/data-use-mentions-extended huggingface dataset:
Pakistan) are managed by the state— big decisions on finance, employment and pricing are all taken out of the DISCOs’ hands and instead are taken at a higher level. The incentives for management to improve performance are weak. Management is restricted in what it is allowed to do, and there is no corporate penalty for poor performance because of the way in which circular debt has been underwritten by the government’s actions.

Governance indicators for the private utility KE look to be considerably stronger than those for LESCO across all aspects considered, indicating a higher degree of managerial autonomy in this

> 41 For the detailed utility management index, see the annex.

40
transfer payments, both domestic and overseas remittances, in most analyses of trade and poverty are not well fleshed out and deserve greater attention in the future.

# **VIII.  Conclusions**

One of the most lively areas of development economics research in recent years involves assessing the micro-economic implications of macro-level policies – particularly those related to international trade. The 2003 volume edited by Bourguignon and Pereira da Silva sets out the current range of tools available for evaluating the poverty impacts of economic policies. These editors conclude that, while there is a wide range of research methodologies available for assessing the microeconomic incidence of micro-policies, and similarly many tools for assessing the impact of macrolevel policies on markets and broad groups of “representative” households, there is a gap in the current literature when it comes to eliciting the disaggregated household and firm level impacts of trade and other macro-economic policies. Recent research aims to address this gap in our knowledge and the present survey offers an overview of this literature.

Many of the most recent and innovative studies sequentially link the top-down and bottom-up approaches in a two-step procedure, such that general equilibrium mechanisms are incorporated along with detailed household survey information. While not necessarily elegant in a theoretical sense, this approach accounts for the majority of trade-poverty linkages, is based on solid empirical foundations, and is compatible with both single and multi-region trade modeling. With time, we expect the degree of integration between micro- and macro-analyses to become tighter, with fully integrated general equilibrium models eventually becoming the norm at both the national and global levels.

This review highlights the critical role of factor markets in determining the poverty impacts of trade policies. The preponderance of the evidence from the studies encompassed by this survey points to the dominance on earnings-side impacts over consumption side effects. This is problematic, since household surveys are notable for their under-reporting of income. From the perspective of the poor, it is the market for unskilled labor that is most important. The poverty impacts of trade policy often hinge crucially on how well the increased demand
percentage points to growth. This was due almost entirely to the introduction of mobile telephony in Ethiopia. Simulations suggest that if Ethiopia’s infrastructure platform could be improved to the level of the African leader, Mauritius, annual per capita growth rates could increase by 3.8 percent. This potential impact would come equally from improvements to transport, power, and ICT infrastructure (figure 1).

Evidence from enterprise surveys suggests that infrastructure constraints are responsible for an estimated 50 percent of the productivity handicap faced by Ethiopian firms. The remainder is caused by governance, red tape, and financing constraints. Power is by far the infrastructure constraint that weighs most heavily on Ethiopian firms (figure 2).

2
Two studies have shown promising results in using non-probability-based surveys, and using statistical methods to make them representative. Goel et al. (2015) employed an online opt-in survey of social and political attitudes. The survey utilized 14 demographic questions and 49 attitudinal questions that were drawn from the 2012 General Social Survey (GSS) and recent Pew Research Center studies. To correct for the biases in the non-representative online data, the study generates population-level and subgroup-level estimates via model-based poststratification [Gelman and Little, 1997, Wang et al., 2015]. After statistical correction, the median absolute difference between non-probability and probability surveys is 7.4 percentage points. The authors find this to be comparable to the difference between various probability surveys themselves, and hence conclude that “non-representative surveys are a promising tool for fast, cheap, and (mostly) accurate measurement of public opinion.” Wang et al. (2015) conduct a series of daily voter intention polls in the Xbox gaming platform. After adjustments using regression and poststratification, the corrected estimates are comparable to estimates from a leading poll analyst that was based on aggregating traditional polls during the election cycle. From these results, the authors argue non-representative polling shows promise not only for election forecasting, but also for measuring public opinion on a broad range of social, economic and cultural issues.

Few studies look at economic variables. Smyk et al. (2020) study Wage Indicators (WI), an online survey in 17 countries and check if they provide wage distributions that match with benchmark data in each of these countries. They use covariate balancing propensity score to reweight the data. While these weights could match demography and human capital endowment of the representative samples, they are unable to match wage distributions from WI to the representative reference samples.

Propensity score adjustment seems to work better than post-stratification in settings where they have been compared directly. Isaksson and Forsman (2003) study political polls in Sweden and find that propensity score adjustment gives more accurate estimates than poststratification weighting. Yeager et
definition** ; **the most effective public policies that address energy poverty will, therefore, be highly conditioned by the definition adopted by the government** . The differences in energy poverty incidence rates between the measures confirm the challenge of identifying sound and precise indicators. If policymakers plan to target those who experience low income and high costs, the lowincome-high-costs measure might be most appropriate. If they want to generate indicators that can be compared across countries, the 10 percent measure might be most appropriate. Suppose the goal is to capture those that under-consume energy in absolute terms or abnormally high energy expenditure relative to the distribution. The M2 and ( equivalized) M/2 measures might be best suited in that case. Finally, since these expenditure-based measures rely on data from the Household Budget Survey (HBS), and this data is only representative at the national, urban, and rural levels, additional geographical disaggregation (NUTS2 and below) is not possible.

**Characterizing energy affordability within the group experiencing income poverty or estimating the intersection between official income poverty and energy poverty poses challenges.** In particular, the above indicators rely exclusively on the Household budget survey, the main source of energy expenditures among households, but use the income reported in this survey. However, official income poverty in Bulgaria, as in other EU countries, relies on the EUSILC survey. A different approach to this problem involves the statistical matching of these datasets (Rude and Robayo-Abril, 2024).<sup>39</sup> Using

39 Through data fusion, they create a unique dataset incorporating details on energy spending shares, incomebased poverty indicators, inequality measures, and additional variables related to households' living conditions 25
interventions, has observed.<sup>26</sup> But the effects of any future expansion of the project can be rigorously evaluated—at relatively low cost.

_One Way to Rigorously Measure the Impacts of the MVP_ A rigorous impact evaluation of the Millennium Villages can be conducted in the future. One good way to do this is to randomize treatment between members of several matched pairs of village clusters. First, several pairs of village clusters would be chosen using a systematic matching procedure to resemble each other on a number of observable traits—such as population, average education, and a wealth index. This could be based on existing climate and population data, without additional surveys.<sup>27</sup> Second, only one cluster per pair of clusters would be selected—at random—to receive the package intervention. This eliminates the possibility of subjectivity in the choice of untreated comparison villages. Third, surveys of various development indicators would be performed for all the treated and untreated clusters, at multiple time points such as 0, 5, 10, and 15 years after the intervention began. Differences between the treated and untreated clusters would be scientifically attributable to the intervention. These differences could be measured for all of the indicators in Section 4 above, plus household income, consumption, and assets.

This design would address the weaknesses of the current evaluation protocol we discussed above. It would allow measurement of short- and medium-run indicators of various kinds, make the choice of treated villages clear and objective, make the choice of comparison villages clear and objective, and allow for complete baseline data on both groups. This would allow a rigorous measurement of the overall impact of the entire package, across all treatment sites, relative to no intervention.

> 26 Esther Duflo is a professor of economics at the Massachusetts Institute of Technology. Parker (2010) paraphrases an email sent by Duflo to MVP creator and Columbia University professor Jeffrey Sachs in 2009 stating that in her opinion it was “too late”
subset of households’ heads having the same gender, educational attainment and age. The observed income from that neighbor is then imputed to the corresponding observation in the second round, which represents the first-round log income for that household surveyed in the second round: (4) where is actual first-round observed income for the household chosen through the matching process ii ii2 ii1 ΔΔ̃yy = yy −yy� (4) where described above. ii1 yy� Summarizing, the steps to estimate the “unobserved” household per capita income in the first round are the following:

1. Append first and second round of cross-sectional data and create a fused dataset

2. Harmonize the joint distribution of gender and educational attainment in both surveys 3. Take a sample for the statistical learning stage: 80 percent of the fused dataset defined in the first step 4. Estimate the parameters and select the best lambda through cross-validation 5. Calculate the LASSO linear prediction of the first-round log incomes for all households surveyed in the first round as in equation (3) 6. Obtain the LASSO linear fit of the second-round log incomes for all households surveyed in the second round as in equation (3)

- second round as in equation (3)

- 7. For every household head in the second round, obtain the nearest first-round neighbors by minimizing the absolute difference between and for every observation in the first round mm

- that has the same gender, educational attainment and birth year mm2 ii1

- yy� yy� ii

- that has the same gender, educational attainment and birth year

- 8. Randomly select one neighbor from the list of nearest neighbors based on first-round sampling weights ss

- weights

- 9. Take the observed log income of neighbor ( ) chosen in the first round, and assign it to observation surveyed in the second round ( ) ss1

- ss yy

- 10. Estimate movements in-out of poverty and other income dynamics mm1 ss1

- mm yy� = yy

- 11. Repeat 100 times all steps 3 to 10

This process
There is a very consistent pattern that arises from the three data series. The average growth rate in civil war countries during peace gets very close to the average growth rate of peaceful countries. However, these countries grow much more slowly during violent periods. In other words, on average they would not fall behind economically if their recovery period was long enough. In this view it is not recovery in itself that is the problem but the fact that it does not last.

Since this is a core finding we propose several additional ways to illustrate the importance of fragility. First, we develop a measure for the fragility of peace. One, extremely simple, way is to calculate: which provides a number between 0 and 1. This number indicates the likelihood that a year of peace is followed by another year of peace. If this number is high it means that peace in the country was very persistent. Low persistence is an indicator of fragility. Since the calculation of persistence relies on rare events (the start of an armed conflict) it will vary considerably regarding to the sample period and definition of conflict used. In order to include as much violence as possible we use data on all internal PRIO armed conflicts since the second world war to calculate the persistence of peace. Figure 6 shows how persistence of peace, defined this way, relates to GDP per capita now. There is a striking positive relationship. Countries with a high persistence of peace have a much higher GDP per capita than countries with low persistences. This relationship holds despite the fact that we excluded a set of relatively rich countries which never experienced armed conflict.

We use the persistence of peace to explore country variation in GDP per capita. We run a regression, not reported here, of log GDP per capita in 2013 on the persistence measure.<sup>15</sup> The persistence of peace and log GDP are strongly associated: the estimated coefficient of the persistence measure is around 4 and it is statistically significant. A coefficient of
# 2012; Hyde and Marinov, 2014; Borzyskowski, 2013).

More generally, a number of political scientists argue that bad governance, abuse of power, and grievances stemming from political suppression are the principal causes of civil conflict (Schock, 1966; Hegre et al., 2001; Henderson and Singer, 2000; Tucker, 2007).<sup>1</sup> While there is strong evidence of a positive association between elections and civil conflict (Weidmann and Callen, 2013), this association could potentially be due to cultural, historical, or institutional factors. Nevertheless, international donors spend substantial amounts on election monitoring and related programs in an effort to dampen civil conflict and its attendant ills (Kelley, 2008).

Understanding whether and how elections can lead to violence is thus an important issue relevant to development policy. Civil conflict is a major impediment to development and poverty-reduction (World Bank, 2012). Its effects include reductions in economic growth (Abadie and Gardeazabal, 2003), educational attainment (Leon, 2012), height-for-age Z- scores (Akresh et al., 2012), and birth weight (Mansour and Rees, 2012). According to the World Bank (2012), “[p]overty reduction in countries affected by major violence is on average nearly a percentage point slower per year than in countries not affected by violence” (p. 59). The enormous potential gains from ending or preventing civil conflict have led development researchers and practitioners to renew their focus on better understanding its causes and developing prescriptions for effectively addressing it.<sup>2</sup> This study examines whether elections narrowly won by incumbents are associated with post-election violence in an existing civil conflict between government security forces and insurgents.<sup>3</sup> The analysis is based on data from the 2007 Philippine mayoral elections, the

> 1For instance, Tucker (2007) argued that election fraud galvanized the public, triggered protests, and eventually led to the so-called
information of the firm demand of employment categories such as directors, specialized workers (engineers, professionals), administrators, blue-collar operatives, and maintenance services workers. The firm data from the ENIA is combined with administrative customs data on firms’ exports. This allows us to link the exporting status of a firm with the demand for skilled tasks and to track this link for several years. We show that Chilean exporters utilize more skills than Chilean non-exporters. However, the skill composition of employment matters. In particular, we show that exporters require the services of skilled specialized workers (engineers) as opposed to skilled administrative workers or managers. In addition, exporters demand less unskilled labor, especially blue-collar operatives. This suggests that exporters substitute skilled for unskilled labor in the provision of certain skill-intensive tasks used in production. We establish these results with an instrumental variable estimator, where we instrument the firm’s exports (as a share of total sales) with the weighted average of the changes in the exchange rate of all the firm’s international partners (Brambilla, Lederman, Porto 2012; Park, Yang, Shi and Jiang 2010; Verhoogen, 2008). We argue that our results thus estimated provide causal evidence of the skilled tasks demanded by exporters relative to non-exporters.

Our results contribute to a rather succinct literature on tasks utilized in exports. The theory on organizational structure and layers of employment launched by Caliendo and Rossi-Hansberg (2012) has been applied to French data (Caliendo, Monte and

> 1An extended version of this mechanism is the “quality-complementarity” hypothesis. Exports require higher quality products that need to be produced with high-quality inputs (labor, intermediate inputs, machines) at high-productivity firms. See Kugler and Verhoogen (2012) and Bastos, Silva and Verhoogen (2017).

2
A third difference is that while PCRs may compel regulated institutions to supply data, they rarely seem to include data supplied voluntarily from other sources. Of the 57 PCRs surveyed worldwide, only three (France, Slovenia and Taiwan) indicated they received any data on a voluntary basis and in the case of Slovenia, the voluntary data were information received from another government agency. It appears that firms and businesses do not wish to report sometimes sensitive financial data to the government on a voluntary basis in most countries. Important sources of credit data, typically beyond the scope of PCRs, include retail credit, trade credit, microfinance and information from other non-regulated financial institutions such as leasing firms and finance companies or independent credit card issuers.<sup>14</sup> Private credit registries not only seek to expand their access to information from a variety of lenders, but they also dedicate significant resources to obtaining data from other sources, such as court records and diverse public databases, which may not otherwise be readily available.

Another important difference between public credit registries and private credit reporting firms is the distribution (or degree of transparency) of the data. PCRs frequently provide access to data only to those regulated financial institutions that are also compelled to report their data. This practice, known as reciprocity, is followed by 49 of the 57 PCRs in the survey. As a result, not only are non-reporting financial institutions denied any access to the data but also small businesses, non-financial businesses that provide credit and insurance firms, among others, do not typically have access to the data.<sup>15</sup> Limiting access to the data to these groups, which have may have justifiable business reasons for requesting the data including even the data subject’s consent reduces the overall impact of the data and limits the role they can play in contributing to transparency in an economy. In only a handful of countries do PCRs share their data with private credit bureaus; this also restricts the development of the credit information industry
These econometric results are consistent with anecdotal evidence that formal sector jobs carry "rents" attached to them, and that these rents underlie some commonly observed private deals. According to several sources, when central placement offices still existed, job seekers used to bribe their staff in order to get access to the vacancies in the system. Now that centralized hiring has been abolished, trade union representatives claim the bribes go to the foremen who are in charge of recruitment at the floor level. Paying bribes of this sort would make no sense if the labor market was competitive. The fact that someone else than the workers themselves (e.g. the foremen) may appropriate part of the rents does not alter the conclusion that these rents do exist.

# 4. The Nature of Wage Rigidity

## a) Real rigidity

Limited knowledge on how private sector wages are determined explains the uncertainty about the potential effects of the 1994 devaluation of the CFA Franc. Numerical exercises based on computable general equilibrium models tended to conclude that the short-run effects of the devaluation on output were positive for any plausible values of the key elasticities of demand and supply for goods and services, as well as for any plausible assumptions on public expenditures. The degree of wage indexation, by contrast, turned out to be crucial, and could lead to negative long-run effects (Bourguignon _et al.,_ 1995). A better understanding of how private sector wages are linked to other nominal variables in the economy, including consumer prices, minimum wages and government wages, is therefore needed.

The link between wages and prices is evaluated in this section using industry-level data for CMte d'lvoire and Senegal over a period of two decades. Data are from the records of formal sector firms kept by the governments of these two countries. These records, known as the _Banques de Donnees Financieres,_ or 19
es**|
|Test T1 >= T2 (unadjusted p-value)|0.141|0.058|0.421|0.442|0.501|0.467|0.245|0.250|0.226|0.194|
|Test T1 >= T2 (adjusted p-value)|0.382|0.173|0.829|0.848|0.914|0.891|0.638|0.647|0.548|0.488|
|Endline control mean|0.|405|0.5|96|0.5|74|0.6|24|0.|040|
|Additional controls|No|Yes|No|Yes|No|Yes|No|Yes|No|Yes|
|(Pseudo)R-squared|0.027|0.361|0.009|0.220|0.014|0.257|0.033|0.388|0.137|0.336|
|Observations|2,382|2,382|2,382|2,382|2,382|2,382|2,382|2,382|1,464|1,464|

_Source:_ Authors’ analyses based on baseline and endline survey data.

_Note:_ Average marginal effects (AME) of binary probit models. For lime, Tigray is excluded since it is not recommended in this region and adoption is zero. Additional control variables identical to those listed in notes of Table 2. Bonferroni-adjusted p-values taking into account correlations between outcomes. One-sided equality tests of T1 and T2 are Wald tests. Robust standard errors in parentheses, clustered at the mws level. Significance levels indicated as following: *** p<0.01, ** p<0.05, * p<0.1.

31
. There is evidence from nationally representative data collected at the early stages of the COVID-19 pandemic in Burkina Faso that the pandemic has reduced economic opportunities, which may limit the employment and earning effects of the intervention. Our observed impacts are therefore suggestive of potentially larger impacts of sustained childcare provision in a more favorable economic climate. Conversely, follow-up child assessments were conducted by phone (not direct observation) due to social distancing protocols, so there is some potential for bias from self-reports. Altogether, these results provide strong indication 20