rafmacalaba/datause-encoder-data huggingface dataset:
# sectors.

In Section 4, I briefly review the empirical literature to the extent that it relates to this paper and then, in Section 5 I make an empirical analysis based on the predictions from my theory using Colombian data for the 1983-1998 period. I analyze the effect of productivity on trade protection by following my theory closely. I confirm that the (4-digit ISIC<sup>4</sup> level) sectoral tariffs are inversely related to the import penetration ratio and import demand elasticity, whereas they are positively related to total factor productivity. The results also indicate that the sectors with more productivity gain (or less productivity decline), as compared to the other sectors, are liberalized less.

In the estimations, I account for the extra channels which I mention above and, more specifically, I account for their elimination which leads to a big decline in tariffs. For this purpose, I allow for a shift in the common terms across sectors over time. I tackle the potential endogeneity of the right-hand-side variables, namely the inverse import penetration to import demand elasticity ratio and productivity, by using instrumental variables. The instruments are the capital to output ratio, materials prices, a measure of scale economies (value added/number of firms), and the TFP of the upstream industries which I confirm to be valid based on a test of overidentifying restrictions and also explain intuitively in Section 5.

My productivity estimates come from Eslava, Haltiwanger, Kugler and Kugler (2004) and they are originally calculated at the firm-level which are then aggregated to the 4-digit ISIC level using production shares of each firm. The dataset has the great advantage of using plant level input and output prices. This enables obtaining good estimates with smaller bias as compared to the majority of the studies which need to employ non-parametric estimations and sector level price due to lack of data.

By showing how trade policy depends on productivity both theoretically and empirically, I provide solid evidence for the endogeneity of trade policy with respect to productivity. Finally, in Section 6, I estimate a system of equations for illustrative purposes. In the system, I correct for the endogeneity of tariffs and show that the positive effect of trade liberalization on productivity can be underestimated when endogeneity bias is not accounted for.

> 4International Standard Industrial Classification, United Nations.

3
statistically significant. Taking the results altogether, there is evidence of debt aversion, mainly due to labeling effects. Given these results, further attempts to estimate a monetary value of the impact of debt aversion becomes relevant in order to draw welfare and policy implications.

# **5 Conclusion**

The results presented in this paper support the hypothesis that debt aversion affects investment decisions with respect to education. When financing their higher education, students shy away from a debt contract, particularly because of the label. In this section we discuss some potential drawbacks of our experimental approach, and suggest future research related to our findings.

A potential problem with our specification is the different wording used to describe debt. In English they correspond to “debt” and “loan”. Informally, when one talks about types of financing, ones talks about debt, whereas the actual contract is a loan. Our survey reflected these differences. When asked to choose between financially equivalent contracts, the actual label was “loan”, whereas the questions that referred to the fixed payment included the word “debt”. An alternative hypothesis is that loan aversion is different from debt aversion. Further study allowing for this difference would shed light on this question.

One practical constraint experienced in this study was its small sample size. The experiment was designed with this restriction in mind. For instance, our goal of identifying differences in the preference for one type of contract over another led us to ask questions in the same order across respondents. However, the order of the questions may be an important determinant of students’ answers. If so, then our estimates would be biased. With a larger sample size, randomizing the order of the questions would allow us to control for this issue.

Moreover, before asking students for their preference we could have asked them whether they understand that the contracts they are asked to choose from are financially equivalent. On the one hand, including such question will shed more light on the reason students are observed to have debt aversion. On the other hand, the inclusion of such question will be artificial in the sense that in the real world setting students make decisions without the financial implications being spelled-out for them.

An important shortcoming of this experimental design is that it is a survey, so students are not actually choosing a financial instrument in a real transaction. Research in this direction could provide evidence on the extent to which the findings of this paper hold in a real transaction.

Another avenue of future research is to measure the consequences of the debt aversion 13
create an implausibly large change in the combined HLO score. The end result of this step is to add 54 country‐year observations based on EGRA assessments.<sup>11</sup> Finally, the HLO dataset includes one observation for Sri Lanka in 2013 based on the national assessment, which was linked to TIMSS. These steps result in a combined HLO score with 668 country‐ year observations covering 162 countries. The median country has three time series observations between 2000 and 2017. The HCI is based on a cross‐section of test scores in 2017, taking the most recent test score available in the period 2006‐2017. For 133 of these countries, the most recently‐ available test score falls in the five‐year period 2013‐2017. A cross‐section of most recently‐available test scores are displayed in the bottom panel of **Figure 2** . Test scores range from just below 600 in the best‐performing countries to just above 300 in the worst‐performing countries.

# **A2.3  Adjusting Expected Years of School for Quality**

The next step is to transform test scores into a quality‐adjustment factor for years of school. There are (at least) five options for doing so:<sup>12</sup>

- The first is to exploit the fact that in some settings the same test is administered to children in different grades.  If children in different grades are on average similar in their abilities, the difference in average performance between children in the two grades can be interpreted a measure of the “productivity” of the additional year in terms of higher test scores.  This gradient can then be compared across countries to infer cross‐country differences in average school quality.  One application of this is done directly by PISA, and exploits the fact that PISA tests are administered to children at age 15, irrespective of what grade they are in.  While most PISA test takers are in 9<sup>th</sup> or 10<sup>th</sup> grade (depending on the country), some are in earlier or later grades. Comparing the difference in PISA scores across grades within a country provides an estimate of how many PISA points are gained as a result of one more year of school in that country.

> 11 There is one exception to the rule of giving preference to international assessments over EGRAs.  This is for Yemen, which participated in TIMSS in 2007 and 2011.  Test scores in both years were extremely low (low 200s), and TIMSS caveated the results, noting that too few students achieved minimum performance standards for the country‐level average scores to be reliably estimated.  These TIMSS observations are droped and the 2011 EGRA for Yemen is used instead.

> 12 For an early effort to incorporate cross‐country differences in test scores into measures of human capital, see Caselli (2005), Section 4.2.  Studies such as Hanushek and Woessman (2010) have incorporated tests scores into cross‐country growth regressions.  Hanushek, Ruhose, and Woessman (2015) use test scores as a measure of cognitive ability in a development accounting exercise across US states, and Caselli (2014) performs a similar exercise across countries in Latin America.

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|VARIABLES|Log chan|ge in supportin|g employme|nt, 2007-2010|
|---|---|---|---|---|
||[1]|[2]|[3]|[4]|
|Bartik job change|0.337**|0.348**|0.367**|0.376**|
||[0.153]|[0.142]|[0.163]|[0.152]|
|% White, 2007||0.001||0.001|
|||[0.001]||[0.001]|
|Log of median household income, 2007||0.055||0.043|
|||[0.123]||[0.160]|
|Log of median homevalue, 2007||-0.058||-0.058*|
|||[0.035]||[0.057]|
|% Owner occupied, 2007||-0.005***||-0.005***|
|||[0.001]||[0.002]|
|% With less than high school diploma, 2007||0.000||0.000|
|||[0.002]||[0.002]|
|% With only high school diploma, 2007||-0.001||-0.001|
|||[0.002]||[0.002]|
|Unemployment rate, 2007||0.014**||0.015**|
|||[0.006]||[0.007]|
|Poverty rate, 2007||-0.006||-0.007|
|||[0.005]||[0.006]|
|% Urban, 2007||-0.001||-0.001|
|||[0.000]||[0.001]|
|Leverage, 2006|||-0.008|0.003|
||||[0.013]|[0.018]|
|Constant|0.030|0.400|0.051|0.534|
||[0.027]|[1.091]|[0.039]|[1.263]|
|Observations|3,035|3,035|2,218|2,218|
|R-squared|0.004|0.016|0.005|0.018|

Robust standard errors in brackets (*** p<0.01, ** p<0.05, * p<0.1).

All regressions in this paper are weighted by number of households. Standard errors are clustered at the state level.

# Table 5.1: Baseline results

16
* 33 -

# UNITED **KINGDOM**

Britain's Overseas Development Administration (ODA) maintains data primarily in distribution categories such as geographical areas, multilateral and project aid, training, and technical cooperation. There is no comprehensive health/nutrition/population sectoral summary. Water supply and sanitation (which some donors include in "Health") are included in the category of "Environmental Amenities".

Although ODA is considering a health sector review, there is no current document that can provide official co .prehensive trends. Health totals are thought to be between S68 and S85 million annually (Patten 1988).

Using the current portfolio of bilateral health and population programs, and official data in "British Aid Statistic 1983-87" and the 1987 ODA Annual Review, health and maternal health expenditures have been estimated. The estimates are based on a number of assumptions that permit comparability with other donors:

- Bilateral project aid is included for health, nutrition, and population programs. Each multiyear project expenditure is divided by the number of years for project duration to obtain an average annual expenditure. This method yields somewhat higher annual bilateral totals for the sector than reported in "British Aid Statistics 1983-87." Water and sanitation projects have been excluded, although rural water and sanitation may be elements of other bilateral and NGO projects.

- iMultilateral support is included for UN agencies with a significant health component,

- for instance WHO, UNFPA, and UNICEF. For UNICEF and UNFPA, modest annual increases beyond 1987 have bven assumed. Approximately a third of UNICEF contributions are included in SM calculations, erring on the side of a broad SM definition.

- Contributions by NGOs are included where the organization has a specific health or family planning content, such as IPPF.

- Special contributions for medical and population research are included. Maternal health components are estimated as follows:

- Direct maternal health projects, including facilities (100 percent).

- Family planning (100 percent).

- General health systems and primary health care programs for women of childbearing age (30 to 50 percent).

- Disease control, particularly projects that prevent serious anemia such as malaria (50 percent).

- e Rural sanitatiorn and water projects that help reduce anemia from hookworm (50 percent).

- Medical and population research as applied to maternal health (100 percent).

- Health education (30 percent).
**Table 8. COVID-19 impacts on employment across population groups**

|||Educati<br>|on Level<br>||A<br>|rea<br>|
|---|---|---|---|---|---|---|
||Primary|Lower<br>secondary|Upper<br>secondary|Tertiary|Urban|Rural|
||(1)|(2)|(3)|(4)|(5)|(6)|
|**Panel A: Female**|||||||
|COVID|0.019***|0.038***|0.002|-0.033***|-0.005|0.030***|
||(0.006)|(0.005)|(0.005)|(0.005)|(0.003)|(0.006)|
||[0.009]|[0.000]|[0.899]|[0.000]|[0.326]|[0.000]|
|Observations|664,197|368,681|424,096|183,175|750,197|889,952|
|Pre-pandemic average|0.580|0.394|0.504|0.778|0.515|0.563|
|**Panel B: Male**|||||||
|COVID|-0.025***|0.001|-0.036***|-0.039***|-0.034***|-0.016***|
||(0.004)|(0.005)|(0.005)|(0.006)|(0.005)|(0.004)|
||[0.000]|[0.899]|[0.000]|[0.000]|[0.000]|[0.000]|
|Observations|588,689|369,600|503,616|152,312|730,251|883,966|
|Pre-pandemic average|0.870|0.668|0.819|0.892|0.771|0.843|
|Test:βm= βf(p-<br>value)|0.000|0.000|0.000|0.209|0.000|0.000|

Notes: ***, ** and * denote significance at 1%, 5% and 10%, respectively. Parentheses indicate standard errors of coefficient estimates, while square brackets indicate the False Discovery Rates (FDR). The dependent variable in the regression is the unconditional dummy of being employed. The main variable of interest in the above results is the COVID dummy, which takes on the value of 1 if the time period is August 2020. Control variables in the regression include age, squared age term, marital status, household sizes, education level dummies, training experience dummy, and urban/rural dummy. Fresh graduates are respondents who had graduated during the past year.

38
<!-- Start of picture text --> Percentiles<br>| Average Input Count [J o- 20th<br>Organized Sector Firms 20th- 40th<br>HEacth - Goth<br>aa:eeid aA io om|_| Ne Data r<br>Sree oe<br>| oe |<br>bh o* Chennai ae<br>A 4 0 125 250 S00 750 1,000 ,<br><!-- End of picture text -->
_Figure 1: Energy spending shares (income-based) and energy poverty rates (10 percent threshold) by income quintiles (in percent, 2019):_ <!-- Start of picture text --> 100.0<br>78.4<br>80.0 71.3<br>56.0<br>60.0<br>37.3<br>40.0<br>21.9<br>20.0 18.1 15.7 13.6 10.5<br>7.7<br>0.0<br>Q1 Q2 Q3 Q4 Q5<br>Energy spending share Energy poverty (>10)<br>Percent<br><!-- End of picture text --> _Notes: The graph shows the energy spending share in overall household income at the household level (in percentages) by income quintiles in Blue and the related energy poverty rates in Green. Energy poverty rates use a 0.1 threshold by income quintiles. Energy spending shares are income-based. Income quintile 1 is the 25 percent of households with the lowest average per capita income, while income quintile 5 is the 25 percent of households with the highest average per capita income. We weigh each observation by household survey weights. N=2,952._ _Source: Own estimates based on HBS (2019)._

**We impute energy spending shares from the HBS 2019 into the EU-SILC 2020 (with the income year**

**2019).** Ultimately, we are interested in generating information on energy poverty for households sampled in the EU-SILC. While we could also impute energy poverty indicators directly, imputing energy spending shares gives us the flexibility to explore several expenditure-based measures at once because these measures directly result from energy spending shares.

# **One important caveat is that energy poverty indicators that take a purely monetary perspective**

**suffer from conceptual limitations.** Energy poverty indicators mostly reflect that poorer households potentially spend a larger share of their overall resources on energy and are, therefore, more vulnerable; they suffer from conceptual deficiencies. For example, households that do not have access to energy in the first place might be the most vulnerable ones of all but will likely report lower energy spending shares. Similarly, certain households might access energy generated from illegal logging or private forest fields. These costs are generally not reflected in HBS and might distort official indicators.

18
income elasticities. To circumvent the data constraints, Deaton (1988) developed a technique for estimating price elasticities using cross-sectional household surveys when there is spatial variation in prices. The data requirements to estimate consumers’ behavior are limited to household expenditures by commodity, quantity of each commodity purchased, spatial localization and household characteristics. These variables are usually collected in most household surveys. Deaton’s method assumes no price variations within a spatial location (cluster), and therefore the variation in unit values reflects only quality differentials and measurement errors. Because of available data across time, this paper makes use of both the spatial and time dimensions to identify clusters. This extension circumvents the fact that since many developing countries have data on household surveys that cover several years but are limited in the number of geographical locations, Deaton’s methodology may be inadequate due to the scarcity of geographic clusters in the case of a single household survey.

In this paper I assume that prices do not vary within each year in the same way that Deaton assumes that they do not vary within each geographic location. This assumption implies that the change in prices between years is similar across clusters. Once changes in demand across years are corrected using fixed effects estimators, then the model can be estimated considering each time-spatial location as a separate cluster. This method results in a much larger number of clusters, therefore yielding more precise elasticity estimates.

The essence of this technique can be explained with a one good model.<sup>4</sup> The model is composed of two basic equations. The simplest possible model of demand links the quantity consumed to prices and to the purchasing power of the household (income). Under the assumption that prices do not vary within clusters and that prices are not observable (but unit values are) the model consists of a demand function:

> 4 In the multi-good model the own price elasticities are estimated in the same way. The hurdle is given by the introduction of estimates of cross price elasticities.

4
observed in the phone survey dataset, such potential bias is addressed by controlling for the individual effect _ρi_ also captures. Also, using only the phone survey data set, we do not face issues of attrition bias. Estimates are all weighted by the sampling weights provided with the phone survey to infer results at the national population level.

# **4 Results**

In this section, we discuss the results of the estimation of the effect of COVID-19’s lockdown measures on school attendance after the school system’s re-opening. For convenience, in the rest of the paper, we refer to this effect as the COVID-19 effect.

## **_(i) Baseline Results_**

Table 2 displays our baseline estimations’ results. Panel A displays the results for all 5-18 old. We that COVID-19’s lockdown measures re- respondents aged years find duce school attendance by 6.94 percentage points after the school system’s reopening, and the result is highly statistically significant (Panel A, column 1). Moreover, when we interact the nation-wide lockdown measures with state-specific measures, we find that the severity of the lockdown measures which accompanied schools’ closure has no statistically significant effect on children’s school attendance probability after reopening (Panel A, column 2). These results suggest that the severity of lockdown measures did not make a difference in children’s school attendance probabilities. One possible reason for this result may be a low compliance with these measures, particularly non-binding measures. For example, Bargain and Aminjonov (2021) in a study of several developing countries that work-related the lockdown was find mobility during first period higher among the poor than the non-poor. Additionally, we find no statistically significant differences in the effects of COVID-19’s lockdown measures between rural and urban areas (Panel A, column 3). This finding suggests that the socioeconomic crisis due to COVID19’s lockdown measures did not disproportionately affect children based on their area of residence.

When we break down the above results by age group, we find that schoolchildren 24
# Figure 13: Consequences of Maastricht Fiscal Contraction for European GDP

<!-- Start of picture text --> Real GDP in Europe (Moastricht)<br>0.5<br>@3<br>1.0<br>L.L -1.-0.5 o<br>-20<br>-25<br>-2. -X-X -15 - Germany<br>UIU<br>a)-3.0-1- -U<br>CL ~~~~~~~~~~~~~~~~~~~ --- 2---France<br>-3.5 ~~~~~~~~~~~~~~f-----Italy<br>-4.00 Ed<br>1994 1996 1998 2000 2002 2004 2006 2008 2010 2012<br>Year<br><!-- End of picture text -->
**Table** **<u>8: Determinants of land sale markets participation during last five years</u>**

||**N**|**ER**|**U**|**GA**|
|---|---|---|---|---|
||**Purchased**|**Purchased**|**Purchased**|**Purchased**|
|Land owned five years ago|-0.004***|-0.004***|-0.036***|-0.035***|
||(0.001)|(0.001)|(0.007)|(0.007)|
|Number of adults five years ago|0.005*|0.005*|0.006|0.005|
||(0.003)|(0.003)|(0.006)|(0.006)|
|Age of head/10|-0.001|-0.001|-0.022***|-0.023***|
||(0.003)|(0.003)|(0.004)|(0.004)|
|Head is illiterate|0.000|0.000|-0.015|-0.012|
||(0.016)|(0.016)|(0.020)|(0.020)|
|Head has primary|0.011|0.012|-0.038***|-0.038**|
||(0.016)|(0.016)|(0.015)|(0.015)|
|Female head|-0.019*|-0.019*|-0.038***|-0.039***|
||(0.010)|(0.010)|(0.012)|(0.012)|
|Value of durable goods/1000|0.002**|0.002***|0.000|0.000|
||(0.001)|(0.001)|(0.000)|(0.000)|
|Inefficiency from frontier with manager|-0.009**|-0.009**|-0.013**|-0.015**|
||(0.004)|(0.004)|(0.006)|(0.006)|
|Share of non-ag wage income (EA level)|0.000<br>(0.043)||-0.036<br>(0.050)||
|Distance to the nearest major road/1000||-0.034<br>(0.219)||-0.205<br>(0.742)|
|Observations|2,171|2,171|2,004|1,962|
|Pseudo R-squared|0.056|0.056|0.082|0.083|

_Note:_ Robust standard errors are in brackets. * significant at 10%; ** significant at 5%; *** significant at 1%.

22