rafmacalaba/data-use-mentions-extended huggingface dataset:
was interviewed using the weekly-recall module. In the second month, the sub-sample was split into two randomly assigned groups. The ―treatment‖ group continued with weekly recall surveys for another 4 weeks, while the ―control‖ group was administered a single survey collecting data on the basis of monthly recall at the end of the month. The randomization was privately completed using STATA and was stratified by locality. To check the randomization, we compared household characteristics for the control and treatment groups and found that the two sets of households similar on all observable criteria.

The two data sources are complementary. In the ―observational‖ data – that is, the data from families that were tracked for two years – many individual characteristics are held constant over time, including general healthiness and innate ability to recall events. The large number of observations leads to greater precision in the estimation of recall effects. However, a drawback to using this type of data arises from its vulnerability to temporal autocorrelation of illness patterns that differ between individuals and could systematically influence individuals‘ recollections of events. This temporal autocorrelation would be particularly problematic if the localities in the two different waves differed in their morbidity and treatment seeking patterns. In our analysis, we attempt to tackle this problem by including individual fixed-effects and a full set of monthly dummies. Nonetheless, we cannot entirely rule out the possibility that our results are biased by this autocorrelation.

In the ―experimental‖ data, the autocorrelation of illnesses is entirely controlled for by the randomization process. On the other hand, the experimental sample is not large enough to produce precise heterogeneous treatment effects. In particular, for the observational data, there are a minimum of 36 weekly observations and 5 monthly observations for 300 households, while in the experimental data the sample size is reduced to 4 weekly observations and 1 monthly observation for 205 households. Therefore, we use the experimental data to verify the average treatment effects from the observational estimates, but we rely on the observational data to further examine heterogeneity in the treatment,
41

# <u>Indicator definitions</u>

The first indicator is the incidence of ‘catastrophic’ health expenditures, defined as health expenditures exceeding a certain percentage, _x_ , of a household’s total consumption or income. The 2018 HEFPI database includes two thresholds for catastrophic expenditures (i.e. _x_ ): 10% and 25%. The SDG 3.8.2 indicator is the 10% threshold.

The second indicator is the incidence of ‘impoverishing’ health expenditures, defined as expenditures without which the household would have been above the poverty line, but because of the expenditures is below the poverty line. In the HEFPI 2018 database, we use two absolute international poverty lines ($1.90-a-day and $3.20-a-day in 2011 purchasing power parity (PPP) dollars) and one relative poverty line (50% of median consumption or income).

# <u>Indicator computation</u>

# _Measuring out-of-pocket health expenditures_

Out-of-pocket spending includes not only payments made by the user at the point of use but also cost-sharing and informal payments, both in kind and in cash, but it excludes payments by a third-party payer.

Many household expenditure surveys include questions on health spending, but, being general surveys, most have some shortcomings in terms of identifying out-of-pocket health spending. First, it is sometimes not clear whether the spending reported is gross or net of any reimbursement by third parties (e.g., private insurance company or government agency), in which case out-of-pocket spending could be overestimated. Whenever possible, health insurance premiums should be excluded from out-of-pocket payments, and reimbursement from any type of health insurance scheme should be included to produce a net estimate of out-of-pocket payments. Second, recall periods are sometimes inappropriate, particularly in general expenditure surveys, in which the last 3 months
- 16 -

**Figure 10: Long-term loan holdings (% loan portfolio)**

<!-- Start of picture text --> 1 00%<br>l ~~~~~OConlraclual savings *Nof-l~II I<br><!-- End of picture text -->

**Source:** 1998 OECD Institutional Investors Statistical Yearbook and WB institu;tional investors database.

And finally, contractual savings institutions are also increasingly diversifying risk **015%** abroad as shown in the next figure while the same cannot be said with certainty for non-20% t;1 life insurance companies.

<!-- Start of picture text --> 50%<br>Figure 11: Foreign shares holdings (% loan portfolio)<br>90%<br>1982 1984 1986 1986 1990 1992 1994 1996<br>lContractua savings *No.-Iiel<br><!-- End of picture text -->

**Source:** 1998 OECD Institutional Investors Statistical Yearbook and WB institutional investors database.

In sumnmary, factual evidence based on the data collected shows several differences between contractual savings and non-life insurance companies. Contractual savings can be important institutions in the financial sectors of developed and developing
realized production and any crop losses incurred. In the case of Ethiopia, we furthermore have crop cut data for a sub-sample of plots.<sup>19</sup> The data are available publicly in the World Bank Microdata Library<sup>20</sup> and cover almost 20,000 plots across over 8,000 farms. We complement this data with data from a crop cut and survey experiment, the _Methodological Experiment on Measuring Maize Productivity, Soil Fertility and Variety_ (MAPS) in Uganda. Table 1 summarizes our data sources.

The main unit of analysis for this paper is the plot with separate information for each crop cultivated on the plot. This high level of disaggregation is a feature of our data compared to other approaches that typically analyze losses at the farm level or higher.<sup>21</sup> In Ethiopia, the analysis focuses on two of the major staple crops in the country, maize and sorghum, while in Malawi the paper analyzes maize as the country’s foremost crop cultivated. Furthermore, we also build a plotlevel aggregate of total harvest value on the plot (i.e. across all crops cultivated for every plot of a farm) in local currency units in Malawi to verify the robustness of our analysis to the inclusion of all crop types. The analysis centers around the main agricultural season in each of the two countries, the _Meher_ season in Ethiopia and the rainy season in Malawi. Where applicable, the paper expresses production quantities in total kilogram terms as well as in per hectare terms. The plot sizes used are measured by GPS if available or for small plots with rope and compass in the case of Ethiopia. To correct for outliers in self-reported harvest and input variables as well as our crop losses estimates, per hectare variables are winsorized at the 0.01 percentile.

_Table 1:_ Data sources and sample sizes.

|**Country**|**Data Source**|**Sample Size**|*
<!-- Start of picture text --> Figure 27. Total formal employment by sector, 2014- Figure 28. Total formal employment by province of<br>2022 (FTE) employer registration, 2014-2022 (FTE)<br> 600 600<br> 500 500<br> 400 400<br> 300<br> 300<br> 200<br> 200<br> 100<br> 100<br> -<br>2014 2015 2016 2017 2018 2019 2020 2021 2022 -<br>2014 2015 2016 2017 2018 2019 2020 2021 2022<br>Agriculture, forestry, and fishing Mining and quarrying<br>Rest of industry Non-industrial services Lusaka Copperbelt Other<br>Note: FTE defined as 12 monthly returns to account for Note: FTE defined as 12 monthly returns to account for<br>seasonal employment. seasonal employment. Data on province of employment (as<br>Source: World Bank and ZRA staff calculations based on PAYE opposed to registration location of employer) is not sufficiently<br>database complete for analysis. In some cases (most commonly in<br>agriculture), the employer’s province of registration may differ<br>from actual province of operations. Slight differences in totals<br>with other charts are attributable to completeness of provincial<br>data.<br>Source: World Bank and ZRA staff calculations based on PAYE<br>database<br>Figure 29. Total formal employment by size of firm, Figure 30. Year-on-year change in formal<br>2014-2022 (FTE) employment by driver, 2014-2022 (FTE)<br> 700 120<br> 600 100<br>80<br> 500<br>60<br> 400<br>40<br> 300 20<br> 200 0<br>-20<br> 100<br>-40<br> - -60<br>2014 2015 2016 2017 2018 2019
Filho, Nepstad et al. 2006), this program corresponds to preventing the loss of 12% of the remaining Amazon rainforest in 2014; equivalent to about 55.7 million hectares (138 million acres); and avoiding 10 percent of species facing a high risk of extinction. We estimated the current area of Amazon (in 2014) forests by deducting from the estimate of forest area in 2003 by Soares-Filho (Soares-Filho, Nepstad et al. 2006) deforestation documented in 2004-2014 (PRODES 2015). The area of avoided rainforest loss this scenario concerns, illustrated in yellow in Fig.2, is about 56 million hectares, or about 0.8 times the size of Texas. We find that households in the U.S. and Canada are willing to pay, on average, $92 (95-percent confidence interval $60$124), per household per year (Table 2), to help finance the program.

# _4.2 Aggregate willingness to pay in the U.S. and Canada_

To estimate the total WTP in the U.S. and Canada for the above large-scale program under consideration, we used information from the U.S. Census (Bureau 2016) and Statistics Canada (Canada 2013) to determine that there were about 123.2 million households in the U.S. and about 13.9 million households in Canada in the year of the survey (2014), for a total of 137.1 million households. For Canada, the latest estimate of the number of households is from 2011; we assumed a linear trend in 2006-2011 prevailed when determining the 2014 estimate. Given the total number of households (137.1 million) and using our preferred WTP estimate of $92 per household per year (95-percent confidence interval $60-$124), we estimate an aggregate North American WTP of about $12.0 billion per year for the program discussed above. This estimate corresponds to avoiding the loss of 12% of the remaining Amazon rainforest
production occur in two separate sets of industries that are only related through intra-industry linkages such as the purchase of capital assets. These findings have implications for taxing polluting agencies and subsidizing green outputs.

However, the output approach is less useful for informing skills policy. On the one hand, it leaves out jobs in firms that produce non-green outputs but implement green technologies. For example, a leather manufacturing firm may implement technologies to clean wastewater and may employ workers in charge of this process. On the other hand, it includes all jobs regardless of whether they involve green tasks. For example, it would include the receptionist at a firm producing a filter to purify air. This issue cannot be solved by just restricting the count to production workers since not every worker involved in the production of a green output will perform green tasks or require green skills. For example, while an engineer designing an electric car may require energy efficiency knowledge, most assemblers of such cars may perform the same tasks as assemblers of gas-powered cars.

Moreover, to inform skills policy it is crucial to profile occupations, which reveals an additional limitation of the output approach for this policy objective. Most notably, surveys that are designed to measure green jobs based on their output (or the data that aligns well with this approach) do not collect or link occupational data. Occupational data is necessary to understand the task content and skills requirements of such jobs.<sup>21</sup> In the best-case scenario, analysts would need to work with multiple surveys or databases to adequately inform skills policy.

The U.S., Canada, and the E.U. have good applications of the output approach. In 2011, the U.S. Bureau of Labor Statistics conducted the Green Goods and Services (GGS) survey.<sup>22</sup> The GGS survey was a firmlevel survey on a sample of 120,000 establishments in industries identified as potentially producing green outputs—333 industries out of 1,200 detailed
US$100, is a considerable investment for a dweller in Romania’s rural areas. Our data confirm that renting in Romania is essentially limited to the two highest income quintiles (Table 7).

**Figure 9. Urban Bias: Income Distribution of Young Families in Romania**

<!-- Start of picture text --> 45<br>40<br>35<br>30<br>25 Bucharest<br>Urban areas<br>20<br>Rural areas<br>15<br>10<br>5<br>0<br>1 2 3 4 5<br>Income quintiles<br>Percentage<br><!-- End of picture text --> _Source:_ Household surveys (Table 1).

A recent World Bank report (2004a) draws similar conclusions when discussing the low mobility of households in transition countries compared with developed markets. This report uses household survey data to establish that it is mainly households in the highest income quintile and particularly residents of capital cities that tend to move. And anecdotal evidence from various cities gained during this study indicates that almost all housing supply for such migrants in successful regions is provided by the private rental sector, consistent with the experience of mature economies. However, both results can be interpreted in two very different ways: either they suggest a sufficiently large housing supply elasticity in the successful regions to allow for labor market adjustment and growth, or they simply reflect high turnover rates in a supplyconstrained (rental) housing market segment with little labor market and growth benefit.

The general scarcity of rental housing, absence of new production, and high rent levels presented in this study provides indirect evidence that in many attractive cities in transition countries housing supply constraints dominate migration, not vice versa. Since rental sector supply elasticity depends entirely on mobilizing existing housing stock, not new construction, the outbidding of sitting tenants by migrants crucially determines total migration activity. Examples 34
# **Trade   Liberalization,   Firm   Heterogeneity,   and   Wages: New   Evidence   from   Matched   Employer–Employee   Data**<sup>*****</sup>

Pravin  Krishna _Johns  Hopkins  University  and  NBER_ Jennifer  P.  Poole _University  of  California,  Santa  Cruz_ Mine  Zeynep  Senses _Johns  Hopkins  University_ June  2011

**Abstract**

In  this  paper,  we  use  a  linked  employer–employee  database  from  Brazil  to  examine  the impact  of  trade  reform  on  the  wages  of  workers  employed  at  heterogeneous  firms.   Our analysis  of  the  data  at  the  firm-­‐level  confirms  earlier  findings  of  a  differential  positive  effect of  trade  liberalization  on  the  average  wages  at  exporting  firms  relative  to  non-­‐exporting firms.  However,  this  analysis  of  average  firm-­‐level  wages  is  incomplete  along  several dimensions.  First,  it  cannot  fully  account  for  the  impact  of  a  change  in  trade  barriers  on workforce  composition  especially  in  terms  of  unobservable  (time-­‐invariant)  characteristics of  workers  (innate  ability)  and  any  additional  productivity  that  obtains  in  the  context  of employment  in  the  specific  firm  (match  specific  ability).   Furthermore,  the  firm-­‐level analysis  is  undertaken  under  the  assumption  that  the  assignment  of  workers  to  firms  is random.  This  ignores  the  sorting  of  worker  into  firms  and  leads  to  a  bias  in  estimates  of  the differential  impact  of  trade  on  workers  at  exporting  firms  relative  to  non-­‐exporting  firms. Using  detailed  information  on  worker  and  firm  characteristics  to  control  for  compositional effects  and  using  firm-­‐worker  match  specific  effects  to  account  for  the  endogenous  mobility of  workers,  we  find  the  differential  effect  of  trade  openness  on  wages  in  exporting  firms relative  to  domestic  firms  to  be  insignificant.  Consistent  with  the  models  of  Helpman, Itskhoki,  and  Redding  (2010)  and  Davidson,  Matusz  and  Schevchenko  (2008),  we  also  find that  the  workforce  composition  improves  systematically  in  exporting  firms  in  terms  of innate  (time  invariant)  worker  ability  and  in  terms  the  quality  of  the  worker-­‐firm  matches.

**
10 in the export demand curve, σ is the elasticity of substitution between the exports of country i and those from other countries, and q is the percentage change in the quantity of exports under the scenario with liberalization in the rest of the world excluding the focus country.

All the CGE models referred to below are comparative static, and they assume constant returns to scale and perfectly competitive homogeneous firms and product markets. In all cases other than South Africa (and to a smaller extent for Nicaragua), unemployment is assumed to be unaffected by the trade policy regime. These assumptions are imposed simply because of insufficient data and empirical evidence to impose alternative ones across all the countries being modeled. This use of a standard set of assumptions reduces the risk that differences across countries in results are driven by different assumptions about investment behavior or the degrees of monopolistic competition, firm heterogeneity, economies of scale, or aggregate employment response to trade policy changes (see Helpman, Itskhoki and Redding 2010). Such specifications typically lead to underestimation of the net national welfare gains that would accrue from trade reform though (Francois and Martin 2010). In particular, without dynamics the models will not generate a growth dividend from freeing up markets or from eventual productivity/efficiency gains from trade. Since economic growth is the predominant way in which poverty is reduced in developing countries (see the literature review in Ravallion 2006), the absence of dynamics implies that the results from this study almost certainly underestimate the potential poverty alleviating consequences of liberalization – and might in some situations indicate poverty increases when in fact they would be decreases once the growth consequences are incorporated.

All the country case studies, and one of the two global modeling studies surveyed below, make use of household survey data in addition to a social accounting matrix (SAM). The SAM is the basis for the data in the CGE model, while the household survey data are used in micro-simulation modeling.
have become important drivers of aggregate convergence in labor productivity (Table 1 and Figure 5). This reflects larger productivity improvements in many sectors in EMDEs (especially the LICs) compared to advanced economies as well the fact that many EMDEs experienced rapid sectoral shifts from agricultural sectors over the last few decades.

Looking across the sectors, agricultural productivity growth has been a significant contributor to aggregate convergence, whereas catch-up in other sectors has only contributed a small amount to convergence. Given the share of value-added in the agriculture sector in LICs is large (Figure 1), the strong growth of the agriculture sector has been the most important driver of the aggregate productivity convergence. Our result is in line with Ivanic and Martin (2018) and Ligon and Sadoulet (2018) which illustrate that the increase in agricultural productivity has a larger poverty-reduction effect than increases in other sectors.

# **3.2.3 Sectoral convergence**

The same exercise is undertaken to examine convergence across sectors (Table 2 and Figure 5). Examining this using this study’s extensive data suggests the following:

- **Agriculture sector:** Over the first half of the sample and the over the entire sample, there is no evidence for unconditional convergence in the agriculture sector. This is line with Kinfemichael and Morshed (2019). However, over the second half of the sample (1995-2018) there is convergence. This seems to some degree to be due to the commodity price boom during the 2000s. Nonetheless, the estimated convergence rate is very low, implying that it would take about 750 years for the bottom 10 percent of the productivity level to reach the top 10 percent.<sup>9</sup>

- **Industry sectors (Mining, Manufacturing, Utilities and Construction):** There is evidence of unconditional

- convergence in many of the industry sectors. The finding of unconditional convergence in the manufacturing sector is line with Rodrik (2013) using UNIDO data.<sup>10</sup
different from that between imported and domestic varieties, (ii) Chinese share in total imports of that good is strictly positive, and (iii) the exchange rate pass-through is non-zero.<sup>7</sup> Given our assumption regarding the symmetric elasticity of substitution between imported varieties, , the effect of a change in China’s exchange rate changes vis-à-vis country , , on country ’s imports of a good from country , , does not depend on any exporter attribute. This makes Equation (8) less amenable to empirical analysis. For example, if in order to test the prediction in Equation (8), we were to regress the import demand at the exporterimporter-product level on the Chinese exchange rate vis-à-vis the importing country, we would not be able to include destination country fixed effects. We could, of course, strive to include all the relevant destination country attributes explicitly, but the effect of the exchange rate would not be estimated precisely because we would inevitably fail to control for certain unobserved sources of variation at the destination country (or destination-year) level.

One way to have such more general controls is to introduce more variation—for example, across exporters—in the right hand side of Equation (8). This would allow importer demand at the exporter-importer-product level to be regressed on a term that had all three sources of variation, which in turn would allow the inclusion of general fixed effects in the regression. To find such variation across exporters, we consider country ’s imports, , from country of a particular bundle of goods , defined at a higher level of aggregation. In our empirical analysis, we use trade data at the Harmonized System (HS) 6-digit. Therefore is defined at the HS 6-digit level. Country ’s imports of (at say the HS 4-digit level) can be expressed as:

> 7 Note that in Broda and Weinstein (2006), , i.e. the elasticities of substitution between imported varieties equals the elasticity of substitution between home and