rafmacalaba/datause-encoder-data huggingface dataset:
the one that benefits the most from the creation of electricity infrastructure. This last general equilibrium effect shows up in the OLS estimates.<sup>5</sup> Based on our model simulations, the growth of electricity infrastructure explains 8.3, 28.0 and 10.4 percent of the total variation in the GVA shares of agriculture, manufacturing and services, respectively, observed in the Brazilian economy over the period 1970 to 2006, and is responsible for 32.3 percent of the growth observed in GDP. The predictions also provide a substantial role to changes in the sectoral wedges that determine the size of firms. More specifically, variation in sector-specific operating fixed costs that do not depend on electricity access explain 6.3, 14.4 and 5.5 percent of the Brazilian structural transformation process in the primary, secondary and tertiary activities, respectively. We also find that the increase in this component of the fixed costs prevented GDP from rising an additional 15.6 percent during the period 1970-2006. The remaining variation of the sectoral shares in the model is a consequence of changes in the sectoral TFP variable.

We also run some experiments that relate the model simulations to real-life policies. The first two consider the fall in the Brazilian GDP-share of public capital formation, which includes expenditures on expansion and maintenance of electricity infrastructure, from the average 3.28 percent observed in the 1970s and 1980s to the 0.9 percent observed during 1990-2007. We ask the question of what would have been the effect of maintaining the public-capital formation levels of 1970-1989 during the 1990s and 2000s. First, we achieve this counterfactual through a less partisan view of public spending that generates stronger policy incentives in favor of the public input. The result is an increase of the income share of manufacturing and declines in the shares of the other two production activities. There is also a substantial positive effect on total GDP and production levels. In particular, GDP per capita

> 5This does not mean that OLS obtains less biased estimates than the IV. Notice that OLS suffers from omitted variable and simultaneity problems, and that these simultaneity concerns come from the potential positive influence that increases in output have on investment and public capital formation. Moreover, whereas the additional investment required to finance a better grid infrastructure should be attributed to the effects of electricity access, the increase in electricity capital induced by a higher GDP should not. Given that these two differentiated effects on investment are both demand driven, the IV estimate does not discriminate between them, and at the end, captures mainly the supply driven channel. This feature will prove useful during the model calibration.

6
for products that are unusually heavy and/or not typically shipped in containers.<sup>7</sup> Kellogg and Sweeney (2023) study the effects of the JA on U.S. regional markets for petroleum and related products. They show that transport cost differentials associated with the JA lead buyers on the U.S. East Coast to substitute toward foreign sources, even as U.S. suppliers in the Western Gulf Coast shift their sales towards exports and away from the U.S. East Coast. Although their analysis does not include PR, the behavior they document for petroleum products on the East Coast is similar to what we observe for all sea-shipped final products purchased in PR. The absence of JA-compliant tankers and liquid vessels in our port-of-call data is also consistent with their results.

Francois et al. (1996) use a computable general equilibrium (CGE) model of the entire U.S. to measure the equivalent variation of removing the JA for the U.S. economy as a whole. These authors calculate that the welfare cost of the JA to the U.S. economy was approximately $3 billion in 1989.<sup>8</sup> These CGE estimates would include a significant burden of the JA operating through higher prices for upstream inputs. We lack a credible, up-to-date input-output table for PR, which limits our ability to do economy-wide general equilibrium calculations. Furthermore, attribution among upstream products is difficult because firms can respond to JA trade costs by locating outside of PR entirely, which means that some industries to which hat calculus might otherwise be applied are altogether missing from the data.<sup>9</sup> Our CV calculations thus consider only distortions to purchases by final demand, and 7Our evidence that the composition of PR’s upstream imports is biased against sea-shipped products from all sources is different than the substitution away from U.S.-sourced products that Olney estimates in his sample of all products. These are different samples, but the different results may also be due to PR’s island status making industry location decisions there more sensitive to elevated costs of sea-shipping than they are in the collection of U.S. coastal states that Olney studies.

8Estimates using this methodology also appear in USITC (1991) along with subsequent versions of the USITC report. PR was not considered part of the U.S. economy in the CGE studies cited here.

9The endogenous supply of capital and labor flows also complicates GE counterfactual analysis. PR has seen quite large emigration flows over the last two decades, an outflow that may have been much smaller if a larger set of industries were viable in PR.

6
# **Figure 6: Trends in the concentration index of MDG indicators**

<!-- Start of picture text --> Stunting Underweight IMR U5MR<br>-.5 0 .5 1 -.5 0 .5 1 -.5 0 .5 1 -.5 0 .5 1<br>Concentration index Concentration index Concentration index Concentration index<br>Full immunization Measles ANC4+ SBA<br>-.5 0 .5 1 -.5 0 .5 1 -.5 0 .5 1 -.5 0 .5 1<br>Concentration index Concentration index Concentration index Concentration index<br>Contraception HIV-prevalence HIV-condom Malaria-net children<br>-.5 0 .5 1 -.5 0 .5 1 -.5 0 .5 1 -.5 0 .5 1<br>Concentration index Concentration index Concentration index Concentration index<br>Earliest survey Latest survey<br>.6 .2 .25<br>.5<br>.5 .2<br>.4 .15<br>.4 .3 .15<br>.1<br>.3 .2 .1<br>Population average Population average Population average Population average<br>.2 .1 .05 .05<br>.1 0 0 0<br>1 1 1 1<br>.8 .8 .8<br>.8<br>.6 .6 .6<br>.6<br>.4 .4 .4<br>Population average Population average Population average Population average<br>.4<br>.2 .2 .2<br>0 .2 0 0<br>.8 .25 .6 .8<br>.2<br>.6 .6<br>.4<br>.15<br>.4 .4<br>.1<br>Population average Population average Population average .2 Population average<br>.2 .05 .2<br>0 0 0 0<br><!-- End of picture text --> Source: Authors’ calculations from original DHS and MICS datasets. . The population rate is as a fraction, so e.g. 0.2 means a population average of 20%. This is true also for IMR and U5MR which are typically expressed per 1,000.

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The forcing variable age, ���, is defined in weeks and the cut-off �̅ is the last week of December 1998. Thus, ��� takes the value of 1 for the first week of January 1999, 2 for the second week, and so on. Analogously, ��� takes the value of -1 for the third week of December 1998, -2 for the second week, and so on. ���� is a vector of covariates that includes mother’s education in the main specification. We also estimate an alternative specification that includes the additional controls of father’s years of schooling, mother’s and father’s age, and household size; and ���� is the error term.

For the short-term effects, we use the surveys of 1999 and 2001. We also use surveys from 1998 to 2006 to check robustness as well as the persistence of the effect of the ban. In the short-term analysis, we used the following outcomes: work incidence in paid and unpaid activities, school attendance, and proportion of children ‘only working (in paid activities and unpaid activities)’, ‘only studying (attending school)’, ‘working (in paid and unpaid activities) and studying’, and ‘neither working nor studying’. For binary outcomes, we estimate linear probability models.

For the long-term effects, we pooled the surveys from 2007 to 2014 to look at education attainment and labor-market outcomes when the individuals of the affected cohort were aged 22 to 29. We selected the following outcomes: the likelihood of having completed at least high school, the likelihood of holding a college degree, the likelihood of being employed, the likelihood of being employed in the formal sector, and the log of monthly earnings.

We estimate the effects for each year individually and then pool all years to improve efficiency. When doing that, we added survey-year dummies to Eq. (1) to control for both cohort composition and time effects. This approach is similar to Angrist et al. (2011), Lemieux and Milligan (2008), Dickens et al. (2014), and Lavy (2015a).

The parameter of interest, �, corresponds to the _intent-to-treat_ (ITT) since the analysis is performed for all individuals who belong to the cohort affected by the law. The identification of this parameter depends on the variations in the labor force participation rates of some 14-year-olds in the first half of 1999 driven by the exogenous change in the law. If the law of December 1998 led to a change in laborforce participation, then the outcomes of the cohort who were 14 years old just before December 1998 can be used as counterfactual for the cohort who turned 14 just after the law passed. A key issue in our identification strategy has to do with whether children aged 14 or 15 at the time of the law change would remain eligible to work in the formal sector or that would be conditional on them already working and/or having a working 13
|**Human Development Outcomes**|||||||
|---|---|---|---|---|---|---|
|Life expectancy (years)|50.8|51.3|.062|48.2|*<br>-.136|*|
|Dependency ratio|0.93|.91|-.067<br>*|.93|.053||
|Under 5 mortality (per 1,000)|150.4|145.8|-.108|188.7|*<br>.237|*|
|Infant mortality (per 1,000 live births)|86.2|84.2|-.108|114.1|*<br>.277|*|
|Primarycompletion rate(% of relevant agegroup)|53.2|52.7|.049|40.9|*<br>-.178|*|
|Notes:|||||||

(*) t-test significant at the 5% level. The means of variables are tested against the means of normal times corresponding to the respective periods of growth acceleration or decelerations. However, the sub-sample means of normal times are generally similar to those of the entire period in the second column. See reference below for the details including the corresponding standard errors. Source: Arbache and Page (2007b)

**_Human development outcomes._** Growth variability also affects a number of important human development indicators. Life expectancy is substantially lower in countries experiencing growth decelerations than in countries experiencing normal times. The correlation coefficient is negative, suggesting that more collapses are associated with lower life expectancy. The dependency ratio is slightly lower during growth accelerations, and the correlation coefficient is negative, as expected. Mortality for children under age 5 and infant mortality are substantially higher during growth decelerations than in normal times, but these indicators do not improve during growth accelerations (see box 1). Correlation coefficients suggest that growth collapses are associated with increases in mortality. The primary completion rate is substantially lower in countries experiencing growth decelerations and is negatively correlated with growth collapses.

# **Box 1: Asymmetric impacts of good and bad times on the poor: the case of infant mortality**

During normal times the average infant mortality rate across Sub-Saharan Africa is 86.2 per 1,000. During good times, the ratio falls slightly to 84.2, which is not statistically different. But there is a major increase of infant mortality to 114.1 during the bad times. This evidence is illustrated by the kernel density distribution. During normal or accelerating times the kernel is right skewed (figures 6a and 6b). But during decelerating times the kernel curve is clearly skewed to the left, and a second peak emerges, representing the countries experiencing much worse infant mortality levels (figure 6c).

Among the countries in the second peak are Malawi and Mali in 1980, both of whose infant mortality rate was 176. Remarkably, as growth accelerated these countries experienced substantially lower figures: 115 in 1995 for Malawi and 124 in 2000 for Mali. Other countries in the second peak include Angola in 1990 and 1995, Niger in 1985 and 1990, and Sierra Leone in 1985, 1990, and 1995. These examples highlight the asymmetric relationship between growth acceleration and deceleration and social indicators, suggesting that growth volatility does matter and is marginally more important for the poor than growth acceleration.

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**12 |** P a g e

An examination of data on trade of the wood cluster leads to the following observations: First, total exports of forest 'gate' and wood based products significantly increased over 2003‐07, although at the rates lagging behind the growth of total exports. The value of wood cluster exports more than tripled: their total exports amounted to US$ 706 million in 2007 contributing 17 percent to the total down from 22 percent in 2003 (Table 5).

Second, there are indications of the increase in the level of processing embodied in exports, although products of secondary wood processing continue towering over other wood‐related exports with their share in total slowly decreasing from 88 percent in 2003 to 82 percent in 2007. Note however that although the export coverage of imports increased in logs, it fell in other stages of processing except for most processed other wood products. It might be tempting to argue that BiH ‘wood‐cluster’ export basket should be more oriented towards higher stages of processing. Profitability and value‐ added generated by activity should be the major determinant of allocation of activities to various stages. Viewed in a regional perspective, the composition is neither better nor worse. Secondary wood processed products together with other wood based products accounted in BiH exports (92 percent) roughly for a similar share (91 percent) as in combined exports of Serbia and Montenegro.

Third, the wood cluster has remained one of the major export earners displaying very strong growth in net exports during the current phase. The value of net exports (difference between the value of exports of wood and wood‐based products) increased between 2003 and 2007 almost five‐fold from US$65 million to US$314 million. The average LSG rate of exports forest 'gate' and wood based products in 2003‐07 was 29 percent as compared to 22 percent for their imports.

Recent developments in foreign trade in furniture made of wood, representing a secondary wood processing stage, provide an interesting illustration of broader developments in the wood cluster. In 2006, this subsector recorded its first surplus of US$8 million since 1995. Although imports increased 38 percent in 2007, the increase in the value of exports of 36 percent was sufficiently large to increase next exports to US$10 million (Table 6).

**Table 6: Exports and imports of furniture made of wood in 2001‐06 (in million of US dollars)**

|||||Trade Val<br>|ue($millio<br>|n)<br>|||
|---|---|---|---|---|---|---|---|---|
|SITC‐R3|Product|2001|2002|2003|2004|2005|2006|2007|
|8215|Exports of wood furniture|14|17|16|31|34|47|64|
|8215|Imports of wood furniture|33|37|37|43|41|39|54|
||Difference: exports‐imports|‐19|‐20|‐21|‐12|‐7|8|10|

Source: Based on partners’ data from UN COMTRADE Statistics.
flexibility in providing pensions to workers who have signed contracts, rising demands of workers to receive pension benefits. The results do suggest that employers and rural migrants may perceive an incentive to evade the Labor Law’s requirement that all workers sign contracts.

In Table 11, we present cross-tabulations for employed workers between having a labor contract and being covered by pension and health insurance programs, using data from the 2005 and 2010 waves of the CULS. Most strikingly, social insurance coverage rates are much higher for employees who are local residents than for those who are migrants. In 2005, 77.5% of local resident employees enjoyed pension coverage and 68.9% had health insurance provided by their employers (top panel, Table 11). These coverage rates increased to 88.5% for pensions and 85.8% for health insurance by 2010 (bottom panel, Table 11). For migrant employees, coverage rates for pensions and health insurance increased more modestly, from 22.2% and 20.4% in 2005 to 23.8% and 21.8% in 2010 (Table 11).

How do coverage rates differ with respect to labor contract status? Coverage rates for both local residents and migrants are significantly higher among those employees who have labor contracts, but there is a difference between the two groups in how coverage is associated with labor contracts over time. For migrant employees, the share of those with pension or health care insurance is about twice as great for those with labor contracts compared to those without contracts in 2005, and nearly three times as great in 2010. In other words, the difference in coverage rates for those with and without contracts is more pronounced in 2010 than 2005. However, for local residents, the relative gap in coverage rates for those with and without labor contracts appears to narrow from 2005 to 2010. For both groups, a larger share of those with labor contracts have social insurance coverage in 2010 than 2005, but for local residents the share of those without labor contracts who have coverage also increases, in contrast to a declining share for migrants.

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**<u>Table 7.  Heterogeneous effects by proxy for ability</u>**

||<br>B|<br>Labor<br>usiness|<br>supply<br>Pa|id Work|Lo|an Uptake|
|---|---|---|---|---|---|---|
|Proxy for Ability:|<br>Prob. of<br>Default|Growth in<br>Expenditures|Prob. of<br>Default|Growth in<br>Expenditures|Prob. of<br>Default|Growth in<br>Expenditures|
||(1)|(2)|(3)|(4)|(5)|(6)|
||Tobit|Tobit|Tobit|Tobit|OLS|OLS|
|**Panel A: Intent to Treat Effects**|||||||
|Business Training (1=Yes)|2.624**|-1.473|-2.624|-1.374|0.010|-0.001|
||(1.278)|(0.899)|(2.560)|(1.902)|(0.029)|(0.021)|
|BT x Proxy|-9.056|0.142|30.842*|-2.155|-0.081|-0.002|
||(7.146)|(0.857)|(16.135)|(1.920)|(0.159)|(0.018)|
|Proxy|2.714|-0.456|-86.541***|4.171**|-0.073|0.014|
||(8.067)|(0.779)|(18.106)|(1.785)|(0.153)|(0.015)|
|R-Squared|0.07|0.07|0.05|0.04|0.24|0.24|
|**Panel B: Intent to Treat Effects with Gender Interactions**|||||||
|Business Training (1=Yes)|4.530***|-2.896**|-1.153|-1.107|0.062*|-0.029|
||(1.570)|(1.294)|(2.906)|(2.282)|(0.037)|(0.031)|
|BT x Proxy|-18.835**|1.804|27.109|-3.046|-0.460**|0.040*|
||(8.918)|(1.125)|(19.236)|(2.417)|(0.213)|(0.024)|
|BT x Female|-4.511*|-1.444|-2.762|-2.782|-0.139**|-0.023|
||(2.657)|(2.045)|(5.531)|(4.395)|(0.057)|(0.044)|
|Proxy x Female|-16.526|2.614|47.002|-10.137***|-1.066***|0.051*|
||(12.196)|(1.667)|(28.940)|(3.555)|(0.239)|(0.029)|
|BT x Proxy x Female|23.197|-4.167**|-0.082|5.234|0.987***|-0.095**|
||(14.489)|(1.982)|(33.224)|(4.449)|(0.302)|(0.040)|
|Proxy|9.08|-1.42|-99.395***|6.620***|0.359**|-0.008|
||(8.442)|(0.979)|(19.504)|(2.168)|(0.181)|(0.018)|
|R-Squared|0.07|0.07|0.05|0.05|0.25|0.24|
|P-value of t - test of ...|||||||
|Decision-making BT= BT x Female|0.02|0.15|0.83|0.51|0.02|0.44|
|BT x Ability = BTx Ability x Female|0.05|0.03|0.46|0.17|0.00|0.02|
|Mean of dependent variable among controls with positive hours|1.73|1.73|1.74|1.74|0.48|0.48|
|Percentage of observations among controls with 0 hours|54.78%|54.78%|77.42%|77.42%|-|-|
|N. Observations|3494|3494|3494|3494|4161|4161|

Note: The reported mean of the dependent variable is computed using CO members not offered business training nor assigned to be lottery winners. However, for column 1-4, the mean of positive business and paid work hours is reported. The dependent variable in columns 1-4 is the log of the number of hours. In column 5-6 is a dummy that takes value 1 if individual applied for a loan. In odd-numbered columns the proxy for ability is the probability of default while in even-numbered columns the proxy is the normalized change in log expenditures.See Appendix B for more details on the definition of variables. Column 1-4 is estimated using Tobit and 5-6 is using OLS methods and include as covariates the stratification variables (eligibility for loan lottery, business ownership at baseline, gender and branch dummies). Standard errors reported in parentheses are bootstrapped with 20,000 samples. The following symbols *, * * and ** * denote significance at the 10 , 5, and 1 percent level, respectively.
> - **23** -

Figure **6** KOREA:NEW HOUSING AND Ml, 1966-1983 <!-- Start of picture text --> 7ox - .NAL PAIl Or C. ,_<br>6ox- . ,<br>*ox- I ._ _<br>lO xo ' 91 LI<br>20% - -1W01--<br>lox .<br>6202<br>_3OX- ,,,<br>toss 1970 1974 1978 ;962<br>O Mos,ign1960 P*e4. * MINtelt of Incr4ea<br>Figure 7<br>KOREA: SHARE OF HOUSING iN GNP<br>A41D Ptt CAPITA CNP, 1961-aS<br>6.OX --<br>4-, s.sp /S t<br>3.02-<br>02'O<br>2.02 J<br>82.00 103.00 142.00 246.00 396.00 800.00 1662.00 1600.00 2032.00<br>GNP oor Capita in U.S. OoUcrts<br><!-- End of picture text -->
regression coefficient of the score function for observables in the participation equation ( _X i_ δ in _C_ equation (11) with γ = 0 ) on the corresponding score function for outcomes ( _X i_ β ).

AET argue that their estimator is a lower bound to the true impact when the latter is positive; this rests on the ( _a priori_ reasonable) presumption that the error term in the outcomes equation includes at least some factors that are truly uncorrelated with participation. OLS provides an upper bound. Thus, the AET estimator gives a useful indication of how sensitive OLS is to any selection bias based on unobservables. Altonji et al. (2005b) also show how their method can be used to assess the potential bias in IVE due to an invalid exclusion restriction. One would question an IVE that was outside the interval spanning the AET and OLS estimators.

**_Examples if IVE in practice._** There are two main sources of IVs, namely experimental design features and _a priori_ arguments about the determinants of program placement and outcomes.  The following discussion considers examples of each.

As noted in section 4, it is often the case in social experiments that some of those randomly selected for the program do not want to participate. So there is a problem that actual participation is endogenous. However, the randomized assignment provides a natural IV in this case (Dubin and Rivers, 1993; Angrist et al., 1996; the latter paper provides a formal justification for using IVE for this problem). The exclusion restriction is that being randomly assigned to the program only affects outcomes via actual program participation An example is found in the aforementioned MTO experiment, in which randomlyselected inner-city families in US cities were given vouchers to buy housing in better-off areas. Not everyone offered a voucher took up the opportunity. The difference in outcomes (such as school drop-out rates) only reveal the extent of the external (neighborhood) effect if one corrects for the endogenous take-up using the randomized assignment as the IV (Katz et al., 2001).

An example for a developing country is the _Proempleo_ experiment. Recall that this included a randomly-assigned training component. Under the assumption of perfect take-up or random non-compliance, neither the employment nor incomes of those receiving the training were significantly different to those of the control group 18 months after the experiment began.<sup>52</sup> However, some of those assigned the training component did not want it, and this selection

> 52 The wage subsidy included in the _Proempleo_ experiment did have a significant impact on employment, but not current incomes, though it is plausible that expected future incomes were higher; see Galasso et al., (2004) for further discussion.

44