rafmacalaba/datause-encoder-data huggingface dataset:
12 elasticity of electricity consumption; and (3) the "energy inefficient" economies, comprising the rest of the FSU states, with relatively little (and/or delayed) price adjustment (and with buildup of arrears)--assumed output elasticity of electricity consumption of 1.15 (in the upswing). We label this the conservative elasticity scenario, since it differentiates in such a way to assume increased inefficiency consumption in the FSU (and hence it potentially underestimates the growth of the unofficial economy).

The third scenario--overall conservative--is built on the assumptions that: (1) every unit produced in the (non-Baltic) FSU countries became even more energy-inefficient (by 5 percent) during the transition; (2) the Baltic states remained efficiency-constant in their electric energy use; and (3) the CEE states became 5 percent more efficient in their use of electricity. Hence, this scenario also differentiates according to broad energy-efficiency categories, yet it focuses on overall efficiency ratios (rather than on elasticity differences, which imply differences at the margin).

In summary, three scenarios are to be used empirically to derive estimates of change in overall GDP, as a sort of sensitivity analysis: (1) the unitary elasticity scenario; (2) the conservative elasticity scenario; and (3) the overall conservative scenario.

# **_Official_** _GDP Measures: Just That?_

Since unofficial economy estimates are derived from the difference between overall and official GDP estimates, it is also relevant to note possible measurement biases of official GDP estimates. For our purposes, it is useful that official GDP estimates attempt to measure official GDP, and little else. A possible bias is that the official GDP may not capture some new products produced by official activities, which would result in an overestimate of the unofficial economy emanating from our approach. Conversely, however, official GDP figures do capture, at least minimally, some unofficial activities. Statistical offices, such as Goskomstat, include some minimal adjustments in order to capture at least some unofficial activities. Neither factor is likely to be very large nor subject to major yearly changes in the early 1990s.<sup>22</sup> Since on balance there is no prior data as to which bias would prevail, no further adjustment is made in utilizing the official GDP as the proxy for the official economy.

# _An Empirical Application of the Macroelectric Methodology: The Case of Ukraine_

On the basis of the subtraction of the two variables measuring overall and official GDP growth, respectively, we can arrive at an estimate of the changes in the unofficial economy. We collected data on both official GDP figures and electricity power consumption from 1989 to 1994 for each country from the World Bank and its FSU Statistical Unit. In addition, we conducted research to establish a baseline (for 1989) empirical estimate for the unofficial
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[17] Kaminsky, Graciella, Carmen Reinhart and Carlos A. Végh (2004).<br>“When It Rains It Pours: Procyclical Capital Flows and Macroeconomic<br>Policies.” in NBER Macroeconomics Annual, edited by Mark Gertler and<br>Kenneth Rogoff, Cambridge, MA: MIT Press.<br>[18] Kraay, Aart (2010) “How Large is the Government Spending Multi-<br>plier? Evidence from World Bank Lending,” World Bank Policy Re-<br>search Working Paper No. 5500.<br>[19] Lopez, Humberto and Luis Serven (2006). “A normal relationship ?<br>Poverty, growth, and inequality,” World Bank Policy Research Work-<br>ing Paper Series 3814.<br>[20] Mendoza, Enrique G. and Jonathan D. Ostry (2008). “International<br>Evidence on Fiscal Solvency: Is Fiscal Policy Responsible?,” Journal of<br>Monetary Economics 55(6).<br>[21] Nakamura, Emi and Jén Steinsson (2010) “Fiscal Stimulus in a Mone-<br>tary Union: Evidence from U.S. Regions,” Mimeo: Columbia University.<br>[22] Perotti, Roberto (2004) “Estimating the effects of fiscal policy in OECD<br>countries,” Working Papers 276, IGIER Bocconi University.<br>[23] Perotti Roberto (2011) “The Effects of Tax Shocks on Output: Not So<br>Large, But Not Small Either” NBER Working Papers 16786.<br>[24] Ramey, Valerie A., 2009. “Identifying Government Spending Shocks: It’s<br>All in the Timing,” NBER Working Papers 15464.<br>[25] Ramey, Valerie A. and Matthew D. Shapiro (1998). “Costly capital re-<br>allocation and the effects of government spending,” Carnegie-Rochester<br>Conference Series on Public Policy, 48(1).<br>33<br><!-- End of picture text -->
# **5.1. Reasons behind Differences**

The relevant policy question is thus, what prevents SMEs from engaging in this investment and how could policies be better designed to foster this investment. In some countries, the _Enterprise Surveys_ collected some additional information on the main reasons why firms do not offer job training.<sup>26</sup> Unfortunately, this information is collected for a much smaller set of countries and is subjective (self-reported) which prevents us from using it in our empirical analysis. Figures 2 through 5 report this information for Brazil, China and a set of Central American countries, respectively. The three most important reasons for not offering job training relate to managers thinking that informal training (e.g., through learning by doing) is enough investment to foster productivity, the possibility to hire trained workers from other firms (or the poaching of workers) and the lack of financing opportunities. Nevertheless, these factors are the most important irrespective of firm size. This anecdotal evidence also shows that small firms are more likely to report the poaching of workers/labor turnover, the lack of knowledge or the skepticism about training effectiveness and lack of access to finance than larger firms. Lack of financing comes up as a more important reason not to offer job training for smaller firms than in larger firms in Central America and in Sri Lanka. Also, larger firms are less likely to report lack of knowledge or no need for offering job training than smaller firms.

Even though this evidence is interesting, it is subjective and self reported by those firms not engaging in job training, thus making it difficult to explore as a reliable source of information on the different types of market failures facing all firms. In this section, we will explore the richness in our data set to obtain measurable proxies of the market imperfections impeding this investment. We consider the role of alternative factors discussed above and related with the firm’s access to information, the access to firm

> 26 The exact question posed is differs slightly across countries and for countries in Central America is: “If your plant does not to offer formal training (neither internal or external), please indicate the three principal reasons for not doing so?” (1) New workers become proficient in the job through learning  by doing; (2) Inhouse training is considered adequate; (3) Lack knowledge about training techniques and training programs; (4) Training is not affordable due to my firm's limited resources; (5) Skilled workers can be readily hired from other firms; (6) Skills that workers learn in school are adequate to our needs; (7) Skeptical about the benefits of training and (8) Training is costly because of high labor turnover. Based on this set of options, we have created a dummy variables.

22
et al. (2021a). This index lists five questions on the laws related to the employment of refugees at the country-year level:<sup>21</sup>

1. Does the law or policy contain a provision guaranteeing the right to work?

2. Does the law or policy contain a provision guaranteeing the right to selfemployment and/or to start a business?

3. Does the law or policy contain a provision guaranteeing the right to work in professional fields provided an individual holds the requisite training or certification?

4. Does the law or policy oblige individuals to hold a work permit?

5. Does the law or policy place additional restrictions on individuals in terms of work, including restrictions on which industries they may work in, or where they may work?

We are grateful to the DWRAP authors for sharing these data for their sample in Africa and much of Asia. We supplement these data by coding laws in 20052018 for 33 additional LMIC countries that are not present in the original DWRAP dataset but have GWP data on attitudes. These laws are listed in Table A4, which complements Table A1 in Blair et al. (2021a). We follow the DWRAP methodology and create a 0 to 1 index that combines the five measures according to Anderson (2008). Higher DWRAP indices indicate laws that afford refugees more access to the labor market.

While the _de jure_ environment is important, it does not provide the complete picture. Laws, both liberal and restrictive, are sometimes ignored in practice. Our hypotheses are based on de facto access – what the refugees and host populations actually experience. We are therefore working to create an additional dataset, the 21Questions 1-3 are assigned 0 if no; 1 if yes, only for recognized individuals; 2 if yes, for all individuals. Question 4 is coded 0 if yes, and permits cost a fee; 1 if yes, but permits are free; 2 if no, work permits are not required. Question 5 is coded 0 if yes, at least two work restrictions are in place, in addition to any work permit requirement; 1 if yes, at least one work restriction is in place, in addition to any work permit requirement; 2 if no work restrictions are in place, in addition to any work permit requirement.

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# **INTRODUCTION**

Climatic conditions have a direct impact on the hydrology of a river basin. Climatic change will most likely affect the variability of river flows (Jury and Vaux 2005) and have a variety of additional impacts on the hydrologic cycle (Miller and Yates 2006). The change in variability will affect populations who will no longer be able to plan according to current water availability and supply trends (Milly et al. 2008). Changes will not be uniform and each region will experience either increases or decreases in river discharge compared with present observations (Palmer et al. 2008).

Hydrologic variability creates a significant challenge especially for countries sharing international river basins. Unanticipated high flow events or low flow events may lead to flooding damage, severe drought, and/or fatalities. These events give rise to economic shocks and inter-state political tensions. Such tensions have also been found to take place in the intrastate context including even the likelihood of armed violent conflict increasing after natural disasters (Drury and Olson 1998; Nel and Righarts 2008). In the context of inter-state relations, political tensions may ensue even in basins where mitigating institutions (say, in the form of water treaties) have been negotiated. In other words, climate change could increase the probability of flow below treaty specifications and expectations, leading to non-compliance and consequent political tensions between riparians.

Consequently, when designing a water agreement or appending an outdated one, water negotiators from the respective riparian states need to identify what water flow may look like in the future, in order to design the ideal treaty. Having high quality flow data will also determine the appropriate treaty stipulations and institutional mechanisms that can deal with future challenges. Real time data can also provide policy makers with the ability to predict extreme weather events, and address their impact on an existing treaty.

Flow estimation models are already available to policy analysts, but they need improvement to increase the accuracy of the results. This paper contributes to the growing literature of methodologies with a specific application of the Basist Wetness Index (BWI), which is an index used to identify the magnitude of surface water, for the global set of international river basins. The methodology will predict natural runoff with a greater accuracy and level of significance than precipitation data alone, customary in other methodologies. The method 2
prices.<sup>14</sup> We use the data on imports aggregated by importing firms, their branches, exporting countries, HS eight-digit codes, tariff schemes, and years.

For the empirical analysis, we parameterize the import price equation specified in (13). In particular, we assume that it can be log-linearized as follows: ln pfbcpt = αθfbcpt −βln(1 + Tfbcpt) + ufbcp + uft + ucst + εfbcpt, (22) where if θfbcpt = 0 1 + Tfbcpt = {<sup>1 + MFN</sup> 1 + FTApt<sup>pt</sup> if θfbcpt = 1<sup>.</sup> (23) _pfbcpt_ denotes the import price (average unit value) by branch _b_ of firm _f_ in Thailand for an HS eight-digit product _p_ from country _c_ in year _t_ . _θfbcpt_ indicates the tariff scheme and takes the value of one if an observation is based on an import under the AKFTA and zero otherwise (called the “FTA dummy”). _Tfbcpt_ is the tariff rate in Thailand, which differs according to the tariff scheme used for importing. _MFN_ and _FTA_ are the MFN rates and AKFTA preferential rates, respectively. The coefficient _α_ captures the RoO effect (i.e., _δ_ in Section 1), whereas the coefficient _β_ is related to the tariff effect.

Specifically, the coefficient _α_ indicates whether the rise in marginal costs for RoO compliance by Korean 14 Instead of a model that controls for firm-specific elements, we also estimate a model that takes into account to some extent the decision on FTA use. The estimation results for this case are reported in Table S2.1 in the supplemental appendix.

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Tatyana Bogomolova, Gregorio Impavido, Montserrat Pallares-Miralles

**Figure 23: In a pure DC reform with immediate switching replacement rates* for stock of retirees for teachers will be lower than in the baseline scenario****

<!-- Start of picture text --> 100.0%<br>80.0%<br>60.0%<br>40.0%<br>20.0%<br>0.0%<br>2007 2012 2017 2022 2027 2032 2037 2042 2047 2052 2057 2062 2067 2072<br>Year<br>ref I.1A base<br>Replacement rate<br><!-- End of picture text -->

**Notes** : * Average pension as percentage of average group wage; ** Comparison of replacement rates for stock of retirees for teachers – baseline with Reform I.1A. **Source** : WB calculations based on PROST.

Notice that we are comparing replacement rates produced by the reduced pension in the baseline with the replacement rates produced by the full pension in the reformed scheme. This would appear a rather drastic reduction in post-reform benefits relative to those projected with the generous benefit formula and indexation rules of the current scheme.

The interest rate earned on individual accounts is one of the key factors determining benefits in a defined contribution scheme. To illustrate how sensitive expected benefits are to financial market performance as well as the management of fund reserves, a less optimistic variant Reform I.1B is modeled. Under this scenario, assets accrue a 3% real rate of return. Given the current international experiences in the management of public pension fund reserves, even 3% real rate of return may turn out to be optimistic.

With real wage growth assumptions being the same, the difference between the real interest rate and real wage growth – one of the key determinants of the expected replacement rates – drops to zero in variant I.1B compared to about 2 percentage points in variant I.1A. The two percentage point difference in the assumed real rate of return has a substantial impact on benefits resulting in the replacement rates reduction of up to 12-15 percentage points in variant I.1.B compared to variant I.1.A. The impact of changes in the assumed rate of return on the defined contribution component of old age benefit is illustrated in Figure 24 and Figure 25.

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matter whether we examine different product or income groups only or whether we exclude very small trade flows or trade flows for which previous spells are in the sample. An important avenue for future research is thus to better understand the source of the heterogeneity. It is likely that it can be found in the failure to account for firm-specific characteristics in product level data. In this context, it is interesting that a recent application of a discrete time proportional hazards model to firm level Spanish export data (Esteve-Perez, Pallardo and Requena, 2008) indeed found no evidence for the presence of unobserved heterogeneity.

We now move on to discuss the interpretation of the coefficients in our preferred specification in Table 7, the Prentice-Gloeckler model using a Gamma mixture distribution to summarize unobserved individual heterogeneity. Table 10 contains additional robustness checks on these findings. The results strongly support the prediction that hazard rates are lower for export flows with larger initial values. A 100 percent increase in the initial export value lowers the hazard ratio by about 4 percentage points.<sup>9</sup> The high hazard rate for initially small flows suggests caution in public policy interventions that are aimed specifically at exporters that start small (see also Rauch, 2007). This conclusion is only reversed once all trade flows with initial values smaller than 55000 dollars are excluded from the sample (Table 10). The hazard rate is also shown to increase strongly with distance, with a doubling of the distance between the trading partners resulting in a jump in the hazard by 44 percentage points. Intuitively, we would expect trade costs to be the main driver of this effect. It also appears that colonial ties and in particular a common language and a common border significantly increase the likelihood of sustaining bilateral trade flows over time. Qualitatively, all of these results are consistent with what is found in Besedes and Prusa (2006a) and Blyde (2008). However, the coefficient estimates differ markedly in some cases.

Our results also support the hypothesis that previous experience in exporting is important in maintaining a trade relationship. First and foremost, we find that the occurrence of

> 9 The importance of the initial size of exports is consistent with work by Brenton and von Uexkull (2007) who find that technical assistance targeted at specific export products tends to be more effective, in terms of the subsequent growth of exports, for larger export flows

18
the incident, Russia temporarily banned the import of 17 Turkish agricultural products including fruits and vegetables, poultry and salt; prohibited the sale of charter holidays for Russians to Turkey; and halted construction projects with Turkish firms in Russia, unless a special exemption was granted. Among the population of firms in the EIS registry, only 3 percent were exporters in 2015; moreover, those firms that were exporting were mostly engaged in manufacturing, a sector which was not targeted by the sanctions (Akgunduz et al., 2019). In addition, Russia is not among the highest ranking destinations for exports from Turkey (it ranks 14<sup>th</sup> among all destinations), and less than 1 percent of firms in the registry were exporting to Russia as of 2015. An adverse effect of the sanctions on the survival probability of those firms, if any, would thus have a minimal influence on our estimates. Furthermore, exporting firms are typically larger and pay higher wages, making them less exposed to variations in the minimum wage. Thus, the confounding effect of the Russian sanctions, if any, would lead us to underestimate the effect of the minimum wage on firm destruction.<sup>22</sup> A final consideration in the interpretation of our difference-in-difference estimates is the stable unit treatment value assumption (SUTVA), which states that the control group should be unaffected by the treatment intervention; that is, the control group should not react to the introduction of the new minimum wage. In our context, this assumption would be violated if there are spillovers from cells that are highly exposed to the minimum wage to those that are weakly exposed in a way that triggers firm closure. To provide comfort on the validity of the assumption, we examine whether the exit behavior of firms in low-exposure cells significantly changed after the minimum-wage increase. As shown in Figure 8, the firm exit rate in low-exposure cells (belowmedian exposure) hardly increased after the minimum-wage hike, compared to quarters in the previous years and compared to high-exposure cells. Since cells below the median exposure are still exposed to the minimum wage to some extent, we also examined the exit behavior of firm in cells whose level of exposure is in the bottom 10 percent of the sample of cells. Exit rates in those very low-exposure cells were virtually identical to the rates evidenced prior to the minimum-wage hike. This suggests that spillovers from high-exposure cells to low-exposure cells associated with the minimum-wage hike have been minimal. Even if there were some degree of influence of these

> 22 To further alleviate concerns about the possibly confounding effects of the Russian sanctions, we also ran our estimations excluding firms that were trading with Russia prior to the rise in the minimum wage. Our estimates were virtually identical to our main results with the full universe of firms.<sup>22</sup>

22
female employees relatively higher wages than non-exporters, but female workers earn lower wages than male workers in both exporting and non-exporting firms. However, the ratio of female wages to total wages is lower in exporting firms than non-exporting firms. These differences are statistically significant (see the Appendix).

**Table 2: Size and wages of exporting vs. non-exporting firms**

||**All firms**|**Non-exporters**|**Exporters**|
|---|---|---|---|
|Average number of employed|28.7|19.7|82.8|
|Average number of female employed|15.4|11.9|32.1|
|Female employment share|0.48|0.51|0.35|
|Average wages|4,647|4,076|7,530|
|Average female wages|3,759|3,264|5,974|
|Female-to-male wage ratio|0.95|0.97|0.88|
|Average turnover|1,825,241|963,991|6,924,577|

Source: GEOSTAT Statistics Survey of Enterprises for 2006-2017. Notes: Exporters are firms that exported in at least 1 year of the sample.

Labor market outcomes in terms of employment and wages exist between firms that export to different destinations. Firms that export to the EU or high-income countries tend to be larger than other exporters, in terms of sales as well as number of employees (total and female). They also pay higher wages (total and female). However, the share of female workers in total workers as well as the female-to-male wage ratio is lower for firms that export to the EU or high-income countries than other exporters (see Table 3). These differences are statistically significant (see the Appendix).

**Table 3: Size and wages of exporting firms by destination**

||**Non-EU**<br>**exporter**|**EU exporter**|**Non-HIC**<br>**exporter**|**HIC**<br>**exporter**|
|---|---|---|---|---|
|Average number of employed|22.9|127.1|22.6|119.0|
|Average number of female employed|12.5|52.0|12.3|49.4|
|Female employment share|0.49|0.38|0.49|0.38|
|Average wages|4,376|8,419|4,344|8,304|
|Average female wages|3,525|6,561|3,500|6,472|
|Female-to-male wage ratio|0.96|0.86|0.96|0.86|
|Average turnover|1,325,639|10,187,536|1,299,063|9,472,563|

Source: GEOSTAT Statistics Survey of Enterprises for 2006-2017.

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