rafmacalaba/data-use-mentions-extended huggingface dataset:
Why use case studies rather than analyze larger sets of firms? Our earlier studies (Pohl et al., 1996; Claessens et al., 1997) use financial data for the 500-1,000 largest manufacturing firms in several transition economies to study the restructuring process. Such analysis presents, however, only a partial picture. Many variables used to uncover patterns of adjustment are not part of standard financial reports - - e.g., data on firm input and output prices, managerial profiles, ownership changes, foreign partnerships, quality control. They are nevertheless essential in understanding the causes for firm restructuring and can only be obtained in enterprise visits.

Slovakia is particularly interesting for a number of reasons. A large part of the heavy and arms industries of former Czechoslovakia was located in Slovakia and it thus inherited a relatively unattractive industrial structure. Slovakia also implemented two very different privatization programs. It participated in the first wave of mass-privatization and privatized the remainder of the firms through leveraged management buy-outs or direct sales to (domestic) outside investors.

The paper is organized as follows. Section II compares the speed of restructuring of large Slovak fimns with similar samples from other transition economies. Section III describes the data and the methodology of collecting it. Section IV reports changes in the ownership structure of the firms. Section V documents some of the common restructuring paths observed during company visits. Section VI evaluates the differences in firm performance and their likely determinants. Section VII concludes.

# **II. Restructuring of Industrial Firms in Transition Economies**

Different approaches to restructuring have been extensively debated by policy makers, foreign advisors and academics. However, it is often not clear what is meant by "restructuring." Does restructuring refer to a single firm or the entire economy? How is restructuring different from the normal process of growth and change? How does one measure restructuring? At the plant level? Economywide?

3
12 1961<sup>12</sup> . When the exemption was passed the first group was 16 to 18 years old, while the second was 20 to 22. Individuals in the first group were not yet eligible for service and thus could change their schooling decisions; those in the second group were instead already beyond high school age. The evidence discussed in the previous section supports the view that differences between exempt and non exempt cohorts reflect the effects of exemption status rather than those of confounding factors correlated with exemption.

In rows A to C we look at the short run effects of exemption status. We draw on the 1981 population census which, importantly, was run in October, at the beginning of the school year. Therefore the evidence describes quite precisely the enrollment decisions of the cohorts affected by the exemption. Youths born in 1963-65 were not yet eligible for service (row A). However, the proportion that was still in high school at the 1981 census date was higher by 3.6 percentage points than that of non-exempt counterparts (p-value 0.027; row B). Correspondingly, a lower percentage entered the labor market (row C), reflecting a choice toward schooling consistent with the mechanism that a longer expected working life increases the incentives to accumulate human capital (Ben-Porath (1967), Jayachandran and Lleras-Muney (2009)). Youths born in 1959-61 had been exempt from military obligations soon after becoming formally eligible to serve. In 1981 the percentage of conscripts was lower by 3.5 percentage points (row A), a proportion similar to that choosing education in younger exempt cohorts. The lower conscription rates basically translated into a higher labor market participation rate rather than school enrollment (row C).

The lower part of table (1) draws on the 1991 population census to describe the long run effects of the exemption by comparing outcomes of exempt and non exempt youths belonging to the two cohorts under analysis ten years after the exemption. The census also includes some retrospective information as
# **COVID-19 and Food Security in Ethiopia: Do Social Protection Programs Protect?**

Kibrom A. Abay, Guush Berhane, John Hoddinott, Kibrom Tafere* _Key words_ : COVID-19, Social Protection, Food Security, Diet Diversity, PSNP, Ethiopia _JEL codes_ : I30, I38, O10, Q18 Corresponding author: Kibrom Tafere, ktafere@worldbank.org, Development Research Group, The World Bank, 1818 H St. NW, Room MC 3-337, Washington, D.C. 20433.

_____________________________________________________________________________________

*Kibrom A. Abay: International Food Policy Research Institute; Guush Berhane: International Food Policy Research Institute; John Hoddinott: Cornell University; Kibrom Tafere: Development Research Group, The World Bank. Acknowledgments: This study was supported by funding from the CGIAR Research Program on Policies, Institutions, and Markets (PIM), which is led by IFPRI, and Research Support Budget (RSB) from the Development Research Group of The World Bank. Berhane and Hoddinott thank the Bill and Melinda Gates Foundation for their funding for work on the 2019 survey (Award No.  OPP1162182). Abay acknowledges funding from the Partnership for Economic Policy (PEP), which is financed by the Department for International Development (DFID) of the United Kingdom (UK Aid) and the International Development Research Centre (IDRC) of Canada. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent.
Table 5: Analysis of classroom quality, teacher, and structural characteristics on children’s social <u>competence</u>

||no|DV: Social|competence|(Raw score)<br>w/ teacher||
|---|---|---|---|---|---|
||<br>controls|w/ controls|w/ teacher|<br>& structure|IV|
||(1)|(2)|(3)|(4)|(5)|
|**Observed classroom quality**||||||
|ECERS-R|0.150***|0.096*|0.083|0.070|0.111*|
||(0.051)|(0.053)|(0.052)|(0.052)|(0.063)|
|**Teacher characteristics**||||||
|% of teachers w/ sr. secondary edu.|||0.825**<br>(0.335)|0.826**<br>(0.336)|0.808**<br>(0.340)|
|% of teachers w/ post secondary edu.|||1.103***<br>(0.347)|1.086***<br>(0.351)|1.073***<br>(0.356)|
|Mean years of teaching|||-0.005|-0.006|-0.007|
||||(0.009)|(0.009)|(0.009)|
|% of teachers w/ no ECED experience|||0.089<br>(0
follow-up action from the government, and if so, what these actions may be. In particular, the link between mandated government action on vaccination and previous experience with drastic population control policies has often led to a fundamental “trust deficit” that impinges and defines survey evidence to this date. See for instance Jegede (2007) on the Nigerian boycott of the Polio Vaccination Campaign or Hussain et al (2012) on continuing misinformation about polio vaccines in India leading to population resistance.<sup>2</sup> Further, the act of surveying in itself could change the surveyed populations’ behavior in the future; a hypothesis for which there is now some evidence. See Zwane et al. (2011) and Das and Leino (2011).

Second, what does informed consent really mean in a low literacy setting? Is consent really informed consent when the respondent does not fully understand the context of the research at hand? The broad notion of informed consent has, to our minds, an implicit social contract where the researcher believes that survey information will provide a better basis for decision making or deepen our understanding of the needs of the surveyed populations in the future. Actions stemming from the research will arguably help improve the lives of at least a subset of the surveyed population. But what should we do in cases where the surveyed population itself engages in practices that are not beneficial—and even harmful—to a broader population of individuals? We have in mind here, for instance, surveys of service providers, including teachers, doctors and licensing organizations. A number of studies in low-income countries have revealed that the behavior of such agents deviate sharply from that which professional ethics in their chosen profession would dictate and the neutrality of the survey team

> 2 Hussain et al (2012) note for instance: “ _Though most respondents supported the eradication program and vaccinated their children, many did not seem informed why the program had intensified the frequency of vaccination. Families described that when they asked the door-to-door vaccination teams why
these countries may have experienced an increase in capital in‡ows which could have come to fuel the credit boom in some of our sample countries. To account for capital in‡ows received by the domestic banking system we include the foreign exchange reserves held at the central bank, scaled by GDP.<sup>9</sup> Last, banking crises are accounted for, by including a dummy that takes value one in crisis inception years and the following two years,<sup>10</sup> with a negative e¤ect expected on credit to GDP.

The analysis uses quarterly data covering the ten countries listed in Appendix 1 over the period 1995-2005; as set out above, the sample is chosen such that it comprises all countries that were part of the former Eastern European bloc and that now are members of the European Union.<sup>11</sup> During the sample period, seven of these countries reformed their payment systems, with two countries (Poland and Czech Republic) having completed payment system reforms before the start of the sample period and one country (Romania) embarking on major reforms only at the very end of the sample.<sup>12</sup> These countries are included to achieve greater e¢ciency in the measurement of the e¤ect of control variables. Appendix 2 contains the list of variables used and the corresponding sources.

Summary statistics for all variables used in our tests are reported in Table 1. The descriptive statistics reported in the ...rst panel con...rm an increase in ...nancial intermediation over the sample period accompanied by a decline in the currency over demand deposits ratio and a small increase in the excess reserves over total deposits ratio.<sup>13</sup> The second panel reports a correlation matrix for a number of control variables. The correlation is high among some of these variables. Our approach is therefore to check the robustness of our results to the inclusion of alternative sets
**Figure 33. Complexity of Services and the Rule of Law, 2011**

<!-- Start of picture text --> .3 .3<br>.2 .2<br>.1 .1<br>BRA BRA<br>IND IND<br>KOR KOR<br>RUS<br>RUS CHN CHN<br>IDN ZAF IDN<br>0 0 ZAF<br>0 20 40 60 80 100 -2 -1 0 1 2<br>Rule of law Quality of Education<br>S hare complex services (% total) S hare complex services (% total)<br><!-- End of picture text --> _Source_ : World Bank Trade in Services Database; Governance Indicators. _Notes_ : WEF; BRA = Brazil, CHN = China, IND = India, RUS = Russia, WLD = World, ZAF = South Africa, IDN = Indonesia, KOR = Korea.

57
to identify takeovers (e.g., Todd and Heining, 2020), we are able to identify all takeover events. Having data on takeovers means that we can accurately capture these events even for small firms. Appendix A provides details on specific administrative datasets that were used to construct our sample.

We combine information on takeovers with a matched employer-employee dataset for all Dutch firms and workers covering the 2006–2019 period. This dataset contains each employment spell at the monthly level, including information on earnings, hours, and contract types. To assess the labor market outcomes of workers, we also link to an administrative dataset covering income from various government benefits, including unemployment insurance benefit and social safety net payments.<sup>1</sup> The final employee-level dataset used is an education database, which contains education information for a subsample of workers. While coverage of this dataset is increasing over time (from 47% in 2006 to 71% in 2019), its sample is skewed towards younger, more educated workers. We use an inverse Mincer equation to impute education levels for workers for whom education information is missing. For the full procedure, we refer to Appendix B.

# **2.2 Sample Construction and Matching Procedure**

We focus on takeovers that happened between 2011 and 2015. We make a number of sample restrictions. First, we restrict the sample to takeovers that involve firms that are active in the four years prior to the takeover and that do not experience any firm event (e.g., takeover, merger, etc.) in those intervening years. Second, because we are interested in employee outcomes, we require that both consolidating firms have at least three employees in the year prior to the takeover. This restriction ensures that we eliminate firms with only self-employed individuals and owners. Third, we restrict the sample to takeovers in which both consolidating firms only have one business unit prior to the takeover.<sup>2</sup> Finally, because
creating more middle-class jobs and harnessing the economic potential of women to build back better going forward.

This paper measures the gendered impacts of the COVID-19 pandemic on employment in Indonesia. While the existing literature is replete with studies that focus on the pandemic’s effects on female employment in developed country contexts (Couch, Fairlie and Xu, 2020; Alon et al., 2021; Andrew et al., 2020; Adams-Prassl et al., 2020; Albanesi and Kim, 2021; Kikuchi et al., 2020), few studies focus on developing countries, particularly in the Southeast Asia region. Moreover, this paper also studies the pandemic’s effect on the structure of Indonesia’s labor market by analyzing its heterogeneous impacts on employment across sectors, occupations and population subgroups. In measuring the pandemic’s impact, we employ a seasonal difference-in-differences approach. This approach is akin to that used in identifying “excess deaths” during the pandemic (Karlinsky and Kobak, 2021), in that the pre-pandemic between-season variations are used as a counterfactual for the between-season variations observed during the pandemic. It then becomes possible to attribute the difference between the actual and counterfactual variations to the impact of the pandemic.

Our empirical strategy relies on two identifying assumptions. First, we leverage the exogenous timing of the COVID-19 pandemic since it was largely unanticipated. Second, we assume that, in the absence of the pandemic, the between-season employment outcome variations in 2020 would largely follow the trends observed in the preceding years. For our analysis, we use Indonesia’s nationally representative National Labor Force Survey (Sakernas<sup>2</sup> ), administered biannually by Statistics Indonesia in February and August. We pool all observations from the

> 2 Sakernas stands for _Survey Angkatan Kerja Nasional_ .

3
USD. We include all investments recorded by AidData, which include ODA- and OOF-like flows. Because that dataset covers the period from 2000 to 2014, we use that time span in the regressions. Columns (1) to (3) in Table 8 present the results. As expected, we find a large negative and statistically significant coefficient on the interaction term in all three regression, implying that the incentive effect of policy-selective aid is not present in recipients of large Chinese investments. This result is robust to the inclusion of region-year fixed effect and holds for both our GPS measures, outlier adjusted or not. In Columns (4) to (6) in this table we report results where we apply the same methodology used for China for aid allocated by IDA.<sup>6</sup> We do not find an interaction effect for 6Note, however, the difference that for IDA the financial flows are all ODA, whereas for China they include 22
mistake. Recognizing this, our analysis is conducted both with and without the suspect West Bengal data. Happily, the focus of our analysis – the wage-bill share of non-manual workers – is not particularly sensitive to the treatment of West Bengal in 1984.

2) Inconsistent aggregation - We found that at the 4 digit industry level a large number of industry-state observations were present in some years but missing in previous or subsequent years, apparently due to a policy of aggregating observations across industry classifications in order to preserve confidentiality. This policy is described in ASI documentation. Unfortunately, this aggregation is not performed consistently over time, so that industries seem to pop in and out of the data. Our solution to this problem was to deal with industries at the 3 digit level of aggregation in (state x industry) analysis and to restrict our attention to States in which employment was large enough to avoid confidentiality problems at the three digit level. Previous work on U.S. manufacturing has not been sensitive to this type of aggregation.

# **_Results_**

Table 3 reports changes in relative wages and quantities for non-manual and manual workers for the pre- and post-reform sample periods, 1984-89 and 1990-98 respectively. Recall that nonmanual workers are the higher education, or “skilled” category. During the 1990-98 period, the proportion of non-manual workers in employment increased by 0.10 percentage points per year, while their relative wages increased by 1.07 percent annually. In contrast, during the 1984-89 period the employment share of non-manual workers dropped by 0.23 percentage points annually, while their relative wages increased at a rate of 0.26 percent per year.

The aggregate increase in demand for non-manual workers in the 1990s is evident in the fact that their proportion and relative wage increased at the same time. What accounted for this demand shift? Skill-bias in technological change is one possibility, but not the only one. A shift 16
and overall nationwide decline in NO2 in 2020 due to the pandemic. The effect of the Democratic margin is negative, consistent with the collective inaction thesis. While this result is interesting, there are important robustness checks to this incomplete claim. For instance, we make no effort to disentangle whether these differences are due to more lax orders, or more resistance to orders. These questions are beyond the scope of our analysis.

# **B Other Results**

## **B.1 Night Lights Baseline**

In this subsection we show how the incremental introduction of updated data, satellite instruments, and technical adjustments (including removal of stray lights and inter-calibration) takes us from Henderson et al. (2012)’s results to the night lights baseline we present in this paper (Table 2, Column 2).

Before presenting this correspondence, we describe the difference between instruments and satellites, which is sometimes confusing. We make use of two separate night lights data sets. First, we use data derived from the US Air Force Defense Meteorological Satellite Program’s S7
Policy Research Working Paper 10842

# **Abstract**

Since 2020, many countries in Sub-Saharan Africa have experienced disruptions to agricultural activities due to the adverse effects of multiple global crises. Notably, the Russian invasion of Ukraine caused a surge in inorganic fertilizer prices, which had potentially significant impacts on Sub-Saharan Africa’s agriculture sector given that most countries in the region are net importers of inorganic fertilizers and the Russian Federation is the world’s largest exporter. Using high-frequency longitudinal phone survey data spanning four years from six Sub-Saharan African countries, this paper examines the dynamics of smallholder agriculture against the backdrop of these crises, with particular focus on prices, availability, and use of inorganic fertilizer, as well as the strategies employed by farmers to cope with high fertilizer prices and other accessibility constraints. The results show that inorganic fertilizer prices have increased in the region since 2020, forcing smallholder farmers to adopt coping mechanisms that are less productivity-enhancing, making them even more susceptible to future crises. Specifically, farming households reduced the quantity of inorganic fertilizer applied, by applying it at lower rates or to a smaller area. In some cases, households sold assets or borrowed money to cope with the high prices of inorganic fertilizers. This calls for policies to help smallholder farmers in the region to build strong support systems to be more resilient and better able to cope with the adverse effects of rising inorganic fertilizer prices during polycrises and related shocks.

This paper is a product of the Development Data Group, Development Economics. 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 aamankwah@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
bias if we were to use non-participants as the comparators. To address this concern we use propensity score matching to select the comparison group from the set of non-participants.<sup>11</sup> Predicted values (the propensity scores) from the probit are used for matching.<sup>12</sup> Using a light survey instrument will no doubt leave biases in these estimators.<sup>13</sup> Given that the program is means tested it is tempting to include income as a predictor of participation in matching. The problem in doing so is that we would then be using the outcome variable (income net of DB) as one of the predictors for estimating impact on that same outcome variable! The results are only unbiased if it is assumed that there are no behavioral effects, which is what one is trying to test. It is not clear what one would then conclude from the results. In general, the direction of bias in the impact estimator cannot be determined.<sup>14</sup> To avoid this problem we should exclude income from the probit (using the regression in the Appendix), though then we run even higher risk that we have selection bias based on unobserved variables in the matching.

When we exclude income from the probit used to estimate the propensity scores we find that the mean income (net of DB) of participants is significantly lower than income of the matched comparison group of non-participants. Income minus DB receipts is 1417 Yuan lower for the DB participants (with a bootstrapped standard error of 270 Yuan using 100 replications) while mean DB receipts are 270 Yuan. It is not believable that receiving an extra 270 Yuan

> 11 On the theory of propensity score matching see Rosenbaum and Rubin (1983). For an application to a similar problem to the present one see Jalan and Ravallion (2003).

> 12 We match each treatment household with the five closest propensity scores.  We did not need to drop any observation from the treatment