rafmacalaba/data-use-mentions-extended huggingface dataset:
equal numbers becoming newly displaced and returning in the years that have followed (e.g., TFPM 2017; OCHA 2019; D’Souza et al. 2022; Favari et al. 2022; etc.). However, these stressors have aggravated a number of longstanding problems in the Republic of Yemen that are too sensitive to measure with traditional modalities of data collection, including reports of increased domestic and gender based violence in the country (e.g., Oxfam 2020; the Guardian 2021; etc.); and have also led to an increase in other illegal activities, including reports of diversion of humanitarian assistance (e.g., Salisbury 2017).

In the face of such a volatile environment, data collection on all issues has become sensitive in parts of the country. In particular, DFA authorities have begun to tightly control the collection of data in regions under its control.<sup>7</sup> This control over data collection has further made respondents in DFA-controlled regions hesitant to respond or fully express themselves in a wide variety of surveys (e.g., Alamoyad et al. 2020; etc.). Thus, even what would normally be non-sensitive issues in non-conflict settings can actually become sensitive.

The inability to perform surveys at all across the entire country due to the conflict, the inability of these surveys to address all issues that are critical to policy makers, and the inability of individuals to respond truthfully to those questions even if they were posed have all created significant information gaps for the humanitarian and development response. Aside from intermittent food security assessments that are performed approximately every two years and are painstakingly negotiated with DFA authorities and remote food security monitoring via mobile phone, there is very little householdlevel data collected in the country (e.g., IPC 2018; WFP 2019; IPC 2020: IPC 2022). This leaves significant gaps as to how households are able to cope with the humanitarian disaster, how the private sector has adapted to the decline
Existing studies argue and demonstrate empirically that stricter environmental regulations cause the firms to invest in innovation and adoption of cleaner technologies, which would eventually lead to increased productivity. There is a strong argument that environmental regulations cause technological innovation that will increase productivity and that the productivity gain offsets the costs of environmental regulations (Porter, 1991; Porter and van de Linde, 1995). This hypothesis, popularly known as ‘Porter’s hypothesis’, has been tested empirically by many studies that are discussed in this paper. The empirical results are, however, ambivalent. While earlier studies do not necessarily prove Porter’s hypothesis, more recent studies do. For example, Jaffe and Palmer (1997) investigate whether the stricter environmental regulations in the United States have spurred R&D activities (i.e., increased patents of green/clean technologies) using panel data of manufacturing industries from 1975 to 1991. They find investments in pollution control technologies (i.e., clean technologies) have a significant positive effect on R&D expenditures. However, they do not find strong evidence of the deployment of clean technologies during that period. This is sometimes referred to as a “weak” version of Porter’s hypothesis in the literature because it does not confirm whether innovation or the use of clean/green technologies is good for firms. The result is not surprising, though, as the large-scale deployment of cleaner or greener technologies in local air pollution control occurred after the 1990s. Moreover, increased deployment of greener energy technologies, such as wind and solar, accelerated more recently, after 2005.

Some studies (e.g., Cao et al., 2021; Peng et al., 2021) also examine impacts on the productivity of green/clean investment resulted from environmental regulations in China. Cao et al. (2021) report that regulated firms are more motivated (or obligated) to invest in green/clean technologies to meet existing environmental regulations. Using sample data from environmentally dirty
Figure 5: Average Number of Days Without Rain <!-- Start of picture text --> Ethiopia (n = 10,674) Malawi (n = 8,897)<br>100 140<br>120<br>80<br>100<br>60<br>80<br>40 60<br>40<br>20<br>2010 2015 2020 2008 2010 2012 2014 2016 2018<br>Niger (n = 3,913) Nigeria (n = 9,145)<br>80 80<br>60<br>60<br>40<br>40<br>20<br>20 0<br>2011 2012 2013 2014 2010 2012 2014 2016 2018<br>Tanzania (n = 9,916) Uganda (n = 11,692)<br>120<br>80<br>100<br>80 60<br>60<br>40<br>40<br>20 20<br>2005 2010 2015 2020 2010 2015 2020<br>Year Year<br>ARC2 CHIRPS CPC ERA5 MERRA-2 TAMSAT<br>Days without Rain<br>36<br>Days without Rain<br>Days without Rain<br><!-- End of picture text --> _Note_ : The figure presents the mean number of days without rain ( _<_ 1 _mm_ ) in a year, disaggregated by Earth observation source. Means are calculated by fitting a fractional-polynomial line to the data, with 95% confidence interval represented by shaded area. Each line (Earth observation product) in each panel is constructed using all household-year observations ( _n_ ). Variation in lines do not come from variation in the household data that is paired with the Earth observation data. Rather, variation in lines within a panel is solely due to differences in the number of days without rain reported by the Earth observation source.
from households in LSMS surveys ranges from 37 to 305, with the mean being 137 and the median 130 (Beegle et al. 2010). Arguably the value of public goods and time and leisure should also be included in a comprehensive or “full” consumption expenditure aggregate for measurement of poverty, but in most cases this consumption is excluded. The consumption of publicly provided health and education, as well as the use value of durable goods are currently included in some countries, but excluded in others. These matters have been largely ignored in poverty tracking, but our results strongly suggest that they may be of first order importance.
# **Table 5A: T and Rank Tests for Private vs. Public Banks in Non-GCC Region**

Tests are conducted on annual bank-level data for the period 2001-08. Column 5 shows the p-value of a t-test which tests for the equality of means of the groups (allowing for inequality in variance). Column 6 shows the p-value of the Wilcoxon ranksum test which tests whether the groups are samples from populations with the same distribution. Non-GCC countries are Egypt, Jordan, Lebanon, Morocco, Tunisia, and Yemen. State-led countries are Algeria, Libya, and Syria.

|**Variable**|**Private**|**Public**|**Pvalue for t**|**PValue for Rank**|
|---|---|---|---|---|
|Total Assets|2.1E+06|8.2E+06|0.00|0.00|
|ROA|0.92|0.52|0.00|0.00|
|ROE|11.16|7.57|0.01|0.00|
|Net Interest Margin(Total Assets)|2.27|2.25|0.82|0.89|
|Total Interest Income to Assets|5.85|5.18|0.00|0.00|
|Total Interest Expenses to Assets|3.59|2.98|0.00|0.00|
|Non-Interest Income to Assets|1.35|1.14|0.02|0.02|
|Securities to Assets(All Countries)|19.56|20.74|0.40|0.48|
|Securities to Assets(ExcludingLebanon)|13.88|20.23|0.00|0.00|
|OH Costs to Assets|2.00|1.58|0
**Firm sampling.** Our survey targeted three prominent sectors in manufacturing: carpentry, metal fabrication and grain milling. As revealed by the latest Census of Business Establishments conducted by the Uganda Bureau of Statistics in 2010, these are sectors that: (i) employ a large share of workers and (ii) are not dominated by microenterprises with no paid employees. The first criterion implies that we target sectors that are important for policy, whereas the second criterion allows us to focus on labor relationships and human resource management within the firm, which is a key focus of this paper.

We conducted a door-to-door listing of all the firms in our three sectors in the 52 sampled sub-counties, identifying close to 3,000 firms. For each firm in the listing, we recorded their sector of operation and GPS coordinates. This means that we virtually have geo-coded data on the universe of firms in our sampled sub-counties and sectors.<sup>20</sup> We then randomly selected about 1,000 firms from our listing to be included in the survey, oversampling firms with five or more employees. In firms selected for the survey, we interviewed the owner<sup>21</sup> and all the employees working on the main product.<sup>22</sup> As described in Bassi et al. (2021): (i) compliance with the survey was high at over 90%; (ii) all the results from our survey are appropriately weighted to reflect our sampling strategy.

**Survey design.** Our survey was designed to study firm performance, firm location choices, adaptation to pollution and awareness of pollution as a problem, as well as the role of managerial ability. On firm performance, we collected information on revenues and profits per worker as well as wages. On firm location, in addition to collecting GPS coordinates, we asked the firm owner to indicate the reasons behind their location choice, including also detailed information on how firms access customers
<!-- Start of picture text --> Figure 1. Country correlations between cyclical components<br>of real government spending and real GDP, 1980-2020<br>AE EMDE<br>1.0<br>0.8<br>0.6<br>0.4<br>0.2<br>0.0<br>-0.2 AE Average = -0.06<br>EMDE Average = 0.42***<br>-0.4<br>-0.6<br>-0.8<br>-1.0<br>AzerbaijanChina<br>GreeceNicaraguaEcuadorUruguayGuyanaLiberiaArgentina<br>Antigua and BarbudaBrazilNamibiaEquatorial GuineaLebanonNigerPakistanIndiaBoliviaHungaryJordanKenyaBelarusZimbabweFijiRomaniaSerbiaAngolaQatarCyprusRwandaOmanCongo, Rep.Timor-LesteAfghanistanTrinidad and Tobago<br>SudanTongaSenegalMaliLatviaTuvaluBurkina Faso<br>BahrainCongo, Dem. Rep.BelizeJamaicaPolandBhutanLithuaniaKyrgyz RepublicRussian FederationPapua New GuineaLao P.D.R.VanuatuSyriaCabo VerdeGeorgiaUgandaGrenadaCameroonIndonesiaHondurasMoroccoSurinameTogoSeychellesEstoniaMaltaSri LankaSt. Kitts and NevisDjiboutiSt. Vincent and the GrenadinesIran, Rep. of MadagascarPhilippinesAlgeriaUzbekistanMyanmarBarbadosSouth AfricaParaguayTajikistanLesothoMicronesiaGhanaBurundiSaudi ArabiaBeninTurkmenistanMontenegroPanamaMozambiqueMarshall IslandsBosnia and HerzegovinaMoldovaChadComorosThe GambiaCambodiaColombiaTanzaniaLibyaCentral African RepublicCroatiaTurkeyGabonIcelandEthiopiaKiribatiMongolia<br>NigeriaPortugalIsraelPeruSouth SudanBulgariaEritreaSolomon IslandsCzech RepublicIraqAlbania<br>Haiti<br>SamoaMexicoSt. LuciaSierra LeoneKazakhstanGuinea-BissauMauritaniaCosta RicaBotswanaVietnamEswatiniSlovak RepublicTaiwan, ChinaSan MarinoArmeniaMaldives<br>SloveniaDominican Republic<br>Chile ZambiaItalyNauruSpainMauritiusTunisiaGuinea<br>PalauKuwait DominicaThailandLuxembourg New Zealand<br>SwedenMalaysiaFranceNorwayBelgiumJapanMalawiGermany NetherlandsEl Salvador The Bahamas<br>KoreaIrelandAustriaAustralia Guatemala Brunei Darussalam United Arab Emirates<br>Finland<br>North Macedonia<br>Egypt<br>Singapore United Kingdom<br>Denmark United States<br>Switzerland<br>Canada<br>São Tomé and Príncipe<br>Somalia<br>government spending and real GDP 1980-2020<br>Correlation between cyclical components of real Hong Kong SAR, China<br><!-- End of picture text --> Notes: Black (dark) bars denote AE. Red (light) bars denotes EMDE. Each bar represents the correlation between the (HP) cyclical components of real GDP and real government spending. *, **, and *** denote
to the program. All estimates are weighted to account for the sampling scheme.

Of the original cohort of 7,922 children age 0-4, 86 percent (or 6,774 children) were successfully followed up _in the same barangays_ in the first follow-up survey in 2002 (Round 2) and the second follow-up survey in 2003 (Round 3) (see Table B.1). For cost reasons, we only tracked and attempted to interview children in households whose members migrated to another barangay within the same province (399 children or 5 percent of the sample). Out-migration to a non-sample barangay outside the sample municipality or province was the main reason for attrition (552 children). Another 197 children were lost due to deaths, refusals or incomplete interviews. The overall attrition rate by Round 3 was 9 percent (or 749/7922). This attrition rate is comparable to other longitudinal surveys in developing countries (e.g., Alderman, _et al._ 2001a) though higher ________________ 7 The baseline survey was conducted in April-August 2001; the first follow-up survey was fielded in September-November 2002, and the second follow-up in September –November 2003.

8 Although the pilot barangays were supposed to have received initial ECD project inputs prior to the data collection phase of this study, these project inputs were delayed. As discussed in the section on Data and Methodology, we exclude from our estimation sample all barangays that received project inputs prior to the baseline Round 1 data collection.

9 This classification was based on a list of program barangays provided by the Project Management Office (PMO) and verified with the DSWD field offices in the respective areas.

8
0.4 0.5 0.6 0.7 0.8 0.9<br>Measure of distributional incidence<br><!-- End of picture text --> _Sources_ : Banerjee and others 2008; Wodon 2007. _Note_ : A measure of distributional incidence captures the share of subsidies received by the poor, divided by the proportion of the population in poverty. A value greater than 1 implies that the subsidy distribution is progressive (pro-poor), because the share of benefits allocated to the poor is larger than their share of the total population. A value less than 1 implies that the distribution is regressive (pro-rich).

A key message is that power subsidies will always be highly regressive as long as access is highly regressive. The distributional score presented above (figure 21) can be decomposed into access and subsidy design factors (figure 22). The access factor is related to the availability of electricity in the area where the household lives and to the household’s choice to connect to the network if service is available. The subsidy design factor relates to who is targeted to receive the subsidies, rates of subsidization, and consumption levels. As for the overall distributional score, values higher (lower) than one for access and subsidy design factors are indications that those factors are progressive (regressive).

32
numerous special economic zones (SEZs) and industrial clusters that have sprung up since the reforms are undoubtedly two important engines for driving the country’s growth. This study briefly summarizes the development experiences of China’s SEZs and industrial clusters, based on case studies, interviews, field visits, and extensive reviews of the existing literature in an attempt to benefit other developing countries as well as the broader development community.

**Figure 1.2 China’s GDP Per Capita, 1980–2008**

<!-- Start of picture text --> 5000 GDP per capita (constant 2000<br>USD)<br>4000<br>GDP per capita, PPP (constant<br>2005 international Dollar)<br>3000<br>GDP per capita (current USD)<br>2000<br>1000<br>0<br>1980 1982 1984 1986 1988 1990 1992 1994 1996 1998 2000 2002 2004 2006 2008<br>Source: World Bank GDF and WDI central database Sep 2009<br><!-- End of picture text --> The key experiences of China’s SEZs and industrial clusters so far can best be summarized as gradualism with an experimental approach; a strong commitment; and the active, pragmatic facilitation of the state. Some of the specific lessons include:

- the importance of strong commitment and pragmatism from the top leadership;

- preferential policies and broad institutional autonomy;

- strong support and proactive participation of governments, especially in the areas of public goods and externalities;

- public-private partnerships;

- foreign direct investment and investment from the Chinese diaspora;

- business value chains and social networks; and

- continuous technology learning and upgrading.

**Figure 1.3 China's Exports of Goods and Services, 1980–2008**

3
# IV. Learning losses due to COVID-19

Our final database consists of 35 robust studies and reports documenting learning loss, representing data from 20 countries (see Table 1). Most studies (32) find evidence of learning loss. Of the 35 studies reporting learning loss, 27 reported findings in a comparable effect size format. As shown in Figure 1, most studies found learning losses ranging from 0.25 to 0.12 SD. In five studies, learning losses were even greater. The average learning loss across these studies is 0.17 standard deviation – which equates to over half a school year of learning loss.

8
(2018).<sup>16</sup> We assume a factor of informality on goods that incur VAT of 0.5<sup>17</sup> , estimated exogenously to the model.<sup>18</sup>

# 3.4.4. Water Subsidies

Water users are identified as those households in the survey that report using a publicly provided water source – that is, households that receive either piped water into the yard or dwelling or have access to public taps or a public borehole. Water tariffs are not directly subsidized, but the Rural and Urban Water Supply program provides (to the utility operators) a fixed, on-budget sum annually that is meant to cover network maintenance, investment, and upgrading costs. We assume that without this budget support, utility operators would raise prices so that total revenues collected privately covered these costs as well. For these programs, we allocate the total (scaled) expenditure on these programs according to the urban and rural water users’ share of reported urban and rural water consumption, respectively.

# 3.4.5. Agricultural Input Subsidy

The survey does not identify recipients of free agricultural inputs. We turn to Uganda’s National Service Delivery Survey (NSDS) 2015 to generate a propensity score for acquiring subsidized inputs conditional on being a small-scale crop farmer or livestock farmer. We predict that same propensity score within a similar pool of UNHS households and select UNHS households with the highest propensity scores until the proportion of subsidy beneficiaries in the UNHS (out of the pool of small-scale farming households in the UNHS) matches the proportion of subsidy beneficiaries in the NSDS (out of the agricultural-inputpurchasing pool of households in the NSDS). Given the technique we use to allocate agricultural input expenditures, this allocation can be described as the expected allocation of expected benefits available under the inputs program. We then divide the total scaled expenditure on the program by the total number of simulated recipients to get a per-household subsidy.

# 3.4.6
Figure 3: Main employment treatment effects relative to cash <!-- Start of picture text --> Work vs. Cash<br>Psychosocial wellbeing<br>Psychosocial index | |<br>Phq−9 | |<br>Cohen Stress Scale | |<br>Life satisfaction | |<br>Sociability | |<br>Self worth | |<br>Locus of control | |<br>Stability | |<br>Health<br>Days healthy | |<br>Preferences<br>Risk tolerance | |<br>Time preference | |<br>Cognitive performance<br>Cognitive index | |<br>Math score | |<br>Digit span | |<br>Gender<br>Household power index | |<br>Work rights index | |<br>Consumption<br>Savings | |<br>Loan repayment | |<br>Necessary goods | |<br>Luxury goods | |<br>−0.4 −0.2 0.0 0.2 0.4 0.6 0.8<br><!-- End of picture text -->

**Notes:** This figure plots the point estimates and 95% confidence intervals for each outcome in the work treatment group relative to the cash group. All outcomes are standardized. The scales for PHQ-9 and the Cohen Stress Scale have been reversed from previous tables so that positive values represent better outcomes.

42
estimate the 30A Program impact. The results are presented in Tables A.8 to A.11 in Appendix A. Overall, the estimated program effects on both individual-level and householdlevel outcomes remain similar to those reported in Tables 2 to 4. These findings suggest that our estimates are not biased by the 135 Program effects.

# **5.2. Further robustness analysis**

We conduct a number of additional robustness checks that support our estimation results. First, we perform several falsification (placebo) tests. In the first test, we examine the placebo program effects using the pre-program data, specifically the VHLSSs from 2004 to 2008. We consider 2008 as the post-program year and 2004 and 2006 as the pre-program years. We apply equation (3) to estimate the placebo effect on both individual-level and householdlevel outcomes in 2008. The results, presented in Tables A.12 and A.13 in the Appendix, indicate that the variable 'Program*Year 2008' is not statistically significant in nearly all regressions. It is only statistically significant at the 10% level in the regressions of 'wage job'.<sup>7</sup> In the second test, we exclude the 30A Program districts and allocate the control districts to a placebo treatment using cutoff points derived from the 2006 MOLISA poverty rate. Subsequently, we employ the same model specifications to estimate the impact of these placebo cutoffs on individual and household outcomes. Tables A.14 and A.15 report the effects on the individual-level outcomes at placebo cutoff points at 30% and 40%. It shows that there is only a marginally statistically significant effect of the cutoff point at 40% on health care utilization at the 10% level. We also conduct similar analysis for the household-

> 7 We also estimate the placebo effects when using 2006 and 2008 as the post-program years and 2004 as the pre-program year. The results are very similar, demonstrating that the placebo program has no statistically significant effects on almost all the outcome variables.
by regulated firms, whose participation in cost studies is often voluntary anyway. And even if the data are available, there are likely to be difficult issues of joint cost allocation. OMB’s work collecting the available _ex post_ studies is valuable, and it is to be hoped that OMB revisits the question periodically.

A related question is why certain kinds of regulations are more apt to be studied in retrospect than others. For example, in the earlier HMN survey of comparison studies (Harrington, et al. 2000, Harrington 2006), it was striking how such a large fraction of the _ex post_ studies identified were economic incentive regulations. In part, HMN interpreted this as an avuncular interest on the part of economists, who have chosen to examine these particular policies because they find them more interesting from a professional point of view. In addition, with economic incentive regulations it may be easier to get information on _ex post_ regulatory costs. For cap-and-trade programs, the marginal cost of compliance _ex post_ is equal to the permit price for every participant in the market. For emission-fee programs, the marginal compliance cost equals the unit fee, so it is the same _ex post_ as it is _ex ante_ . The total cost, of course is not quite so easy to get, since one must still estimate the cost of the infra-marginal units. Nonetheless, even total cost is much easier 16