rafmacalaba/datause-encoder-data huggingface dataset:
Table A.1 : Variables and data sources

|Variable|Defnition|Source|
|---|---|---|
|Rainfall|Population-weighted average rainfall by<br>country-year in 100s mm.|Kenji Matsuura and Cort Willmott<br>(2007) and Dell et al. (2012)|
|Irrigation|Proportion of agricultural land that is<br>irrigated by country (average of non-<br>missing country-year observations for<br>the period 2001-2009).|World Bank WDI|
|Simple Tarifs|Simple average of bilateral applied im-<br>port tarifs by country-product-year,<br>SITC classifcation.|UNCTAD TRAINS|
|Weighted Tarifs|Weighted average of bilateral applied<br>import tarifs by country-product-year,<br>based on the share of each source coun-<br>try in total country-product imports in<br>the base year, SITC classifcation.|UNCTAD TRAINS and UN COM-<br>TRADE|
|Imports|Bilateral imports value by country-<br>product in the base year, SITC classif-<br>cation.|UN COMTRADE|

8
Table A14: Impact on finance

|||Took a<br>loan|Saved<br>money|
|---|---|---|---|
|T1|(safe spaces)|-0.014|0.051|
|||(0.030)|(0.063)|
|T1|+ Leaders|-0.032|0.089*|
|||(0.024)|(0.052)|
|T2|(safe spaces + IGA)|-0.025|0.097|
|||(0.024)|(0.066)|
|T2|+ Leaders|-0.021|0.166***|
|||(0.026)|(0.048)|
|T3|(safe spaces + husbands’ clubs)|-0.040|0.050|
|||(0.027)|(0.064)|
|T3|+ Leaders|0.010|0.133**|
|||(0.031)|(0.056)|
|T4|(control spillover)|-0.032*|-0.034|
|||(0.019)|(0.041)|
|T1|= T1 + L|.567|.575|
|T2|= T2 + L|.889|.315|
|T3|= T3 + L|.148|.251|
|T1|= T2|.741|.562|
|T2|= T3|.599|.56|
|T1|= T3|.447|.989|
|T1|+ L = T2 + L|.692|.176|
|T2|+ L = T3 + L|.363|.593|
|T1|+ L = T3 + L|.203|.495|
|N||2,995|2,995|
|Co|ntrol mean|.097|.346|

_Note:_ *** p _<_ 0.01, ** p _<_ 0.05, * p _<_ 0.1, standard errors in parentheses clustered at the locality level. The table presents estimated impacts of our 6 interventions’ combinations and the control spillover relative to the pure control group. The p- values of the difference tests between the treatments are in the second part of the table. All regressions control for the baseline value of the outcome variable, stratification fixed effects, and the following baseline variables: adolescent girl’s age, education level, an indicator for being engaged in an IGA, knowledge of modern contraception, household is rural, household head is female, and at least one household member has an agricultural activity. When the baseline value of the outcome variable is missing, it is imputed and a dummy indicating whether the variable is imputed or not is added as control.

47
# **_Annex: Price Elasticities Used in the Computation of Marginal Cost of Funds_**

**Table A.1.  Guinea (1994): Cross Price Elasticities for Six Food Items.**

||Beef|Palm Oil|Bread|Fresh Fish|Smoked Fish|Local rice|
|---|---|---|---|---|---|---|
|Beef|-0.324|-0.019|-0.021|-0.014|-0.009|-0.096|
|Palm Oil|-0.013|-0.231|-0.015|-0.010|-0.006|-0.068|
|Bread|-0.027|-0.024|-0.423|-0.017|-0.012|-0.123|
|Fresh Fish|-0.026|-0.036|-0.040|-0.616|-0.017|-0.183|
|Smoked Fish|-0.005|-0.011|-0.012|-0.008|-0.183|-0.055|
|Local Rice|-0.135|-0.026|-0.030|-0.019|-0.013|-0.568|

Source : Setym International (1995)

**Table A2. Guinea (1994) :  Cross Price Elasticities for Groups of Food Items** .

||**1**|**2**|**3**|**4**|**5**|**6**|**7**|**8**|**9**|**10**|
|---|---|---|---|---|---|---|---|---|---|---|
|1.Cereals|-0.125|-0.018|-0.010|-0.025|-0.029|-0.015|0.000|-0.003|-0.012|-0.004|
|2.Roots|-0.296|-0.214|-0.035|-0.091|-0.104|-0.055|-0.001|-0.009|-0.043|-0.015|
|3.Grains|-0.215|-0.046|-0.135|-0.066|-0.076|-0.040|-0.001|-0.007|-0.031|-0.011|
|4.Fruits|-0.249|-0.053|-0.030|-0.203|-0.088|-0.046|-0.001|-0.008|-0.036|-0.013|
|5.Vegetables|-0.290|-0.062|-0.035|-0.089|-0.250|-0.054|-0.001|-0.009|-0.042|-0.015|
|6.Meats|-0.267|-0.057|-0.032|-0.082|-0.094|-0.185|-0.001|-0.009|-0.038|-0.014|
|7.Livestock|-0.369|-0.078|-0.044|-0.113|-0.130|-0.068|-0.189|-0.012|-0.053|-0.019|
|Products|||||||||||
|8.Drinks|-0.530|-0.113|-0.064|-0.162|-0.186|-0.098|-0.002|-0.288|-0.076|-0.027|
|9.Oils|-0.279|-0.059|-0.033|-0.085|-0.098|-0.052|-0.001|-0.009|-0.183|-0.014|
|10.Sweets|-0.297|-0.063|-0.036|-0.091|-0.104|-0.055|-0.001|-0.010|-0.043|-0.167|

Source : Setym International (1995) 23
(2) where<sup>_s_</sup> _j_<sup>is the share of seats allocated to the district</sup><sup>_j_and</sup><sup>_v_</sup> _j_<sup>is district</sup><sup>_j_’s share of the</sup> population. Values greater than one denote overrepresentation of district _j_ , and the opposite is true for values smaller than one. The data needed to compute (2) come from Samuels and Snyder (2001) and Snyder and Samuels (2004), as well as from national sources (the Appendix lists these data sources).

# **3.2 Cross-country Panel Data**

We use data on democracy for a panel of eleven Latin America countries<sup>15</sup> , covering the period from 1870 to 2000. Our measure of democracy is the variable _polity2_ from the 2007 Polity IV Project dataset. This indicator is coded taking into account several features of a country’s political institutions, such as the openness and competitiveness of executive recruitment, the constraints placed on the chief of the executive, and the competitiveness and regulation of political participation. It ranges from –10 to +10 with higher values corresponding to better democratic institutions<sup>16</sup> . We normalize the measure so that all its values fall between zero and one.

Some of our cross-country regressions control for per-capita GDP, which we take from Maddison (2005) for all countries but Chile. For Chile, we use data from Díaz et al. (2008) since they provide data for more years than Maddison (2005).

# **3.3 Within-country Data**

Our source for Latin American within country data is Bruhn and Gallego (2010). This source provides data on income per capita, the Gini index, temperature, rainfall, and altitude, as well as a landlocked dummy, for different regions within fourteen Latin American countries<sup>17</sup> . We collected additional within-country information on political parties, electoral outcomes, and on

> 15 The countries included in the panel dataset are Argentina, Bolivia, Brazil, Chile, Colombia, Costa Rica, Ecuador, Honduras, Peru, Uruguay and Venezuela.

> 16 See Marshall, Gurr and Jaggers (2010).

> 17 The countries covered in this within country dataset are Argentina, Bolivia, Brazil, Chile, Colombia, Ecuador, El Salvador, Guatemala, Honduras, Mexico, Panama, Paraguay, Uruguay, and Venezuela.

10
Table 1: Selected coefficients from under-5 mortality rate (In) regressions (1990)

|Column:|1|2|3|4|5|6|
|---|---|---|---|---|---|---|
|Method|OLS|2SLS|OLS|2SLS|OLS|2SLS|
|GDP per capita (In)|-.611<br>(9.71)|_-.596-_<br>(3.67)|-.624<br>(8.16)|-.921-<br>(1.84)|-.616<br>(9.08)|-.829-<br>(2.47)|
|Public health exp.<br>(Ln share of GDP)|-.135<br>(1.78)|-.192-<br>(.742)|-.165<br>(1.73)|-.139-<br>_(.359)_|-.085<br>(.931)|.146-<br>(.374)|
|Local health<br>services (In share<br>of expend)|||.076<br>(1.78)|-.359-<br>(.754)|||
|Access to local<br>health services (In<br>share of pop)|||||-.024-<br>(.227)|.336-<br>(.417)|
|Ad<br>vadiiblea.<br>variables.<br>j|**F**ton**al**<br>em e educa<br>ethnolingui<br>|tion, income ineq<br>stic fractionalizat<br>water, dummy<br>|uality, percent<br>ion index, dum<br>variables for r|urban, dummy<br>my for "tropica<br>egion and a con|for predomina<br>l" country, acc<br>stant term.|ntly Muslim,<br>ess to safe|
|R-squared|.9469|F<br>9465|.9512|.8834|.9608|.9430|
|Num. Obs.|98|98|73||73|75|75|

Notes: White heteroskedasticity-corrected t-statistics are in parentheses. -Instruments are, neighbors' public health spending, neighbors' military spending, whether or not the country's main export is oil, and years since 1776 that the country has been independent), and neighbor's shares of spending on local health (column 4), and access to local health services (column 6). See Appendix A for full results.

_Local outcomes._ A second empirical regularity that would be supportive of PHC is if the availability of primary level health facilities or community health workers had a demonstrable impact on local health status. However, the results on the effect of access to hospitals, doctors, and in particular here, public sector clinics, health centers, and rural health workers on health status is, at best, mixed.

A huge technical problem with empirical assessment of the impact of health facilities is that governments may have systematically placed health facilities. If the government places clinics where health status is worst, then a comparison of health status in localities with and without clinics would _understate_ the true impact of clinics. Conversely, if the government 15
Table D.9. Presidential Candidates with Divergent Ideological Classifications

||Election|Shar|e of Vote|s for|Electoral|
|---|---|---|---|---|---|
||Turnout|Left|Center|Right|Competition|
||(1)|(2)|(3)|(4)|(5)|
|_Panel A. Presidential Election_|_- Discrete_|_Treatmen_|_t Variable_|||
|I(PEPm)_×_I(Post2018)t|0.002|-0.018|-0.003|0.007|-0.004|
||(0.004)|(0.016)|(0.004)|(0.004)|(0.013)|
|q-values|[1.00]|[1.00]|[1.00]|[1.00]|[1.00]|
|R-squared|0.877|0.257|0.785|0.866|0.682|
|Observations|6,561|6,561|6,561|6,561|6,549|
|_Panel B. Presidential Election_|_- Continuo_|_s Treatm_|_ent Variab_|_le_||
|PEPm_×_I(Post2018)t|-0.019|-0.051|0.007|-0.006|0.05|
||(0.015)|(0.029)|(0.011)|(0.022)|(0.026)|
|q-values|[0.249]|[0.247]|[0.497]|[0.497]|[0.247]|
|R-squared|0.877|0.257|0.785|0.866|0.682|
|Observations|6,561|6,561|6,561|6,561|6,549|
|Municipality FE|Yes|Yes|Yes|Yes|Yes|
|Year FE|Yes|Yes|Yes|Yes|Yes|
|Department FE x Year|Yes|Yes|Yes|Yes|Yes|
|Municipal controls x Year|Yes|Yes|Yes|Yes|Yes|

_Note:_ This table presents the results of our main specification in equation 1. I(PEPm) is a discrete variable that takes the value of one if the municipality had positive take-up rates and PEPm is the standardized value of the ratio of PEP migrants to population. Electoral competition was estimated following Chac ́on et al. (2006):1 - (% winning candidate - % second-place candidate). The estimates include municipality, electoral year, and department electoral-year fixed effects, and they control for the interaction between electoral year dummies and a set of predetermined municipal characteristics, measured before the beginning of our period and listed in Table C.2. Clustered standard errors at the municipal level are reported in parentheses and False Discovery Rate (FDR) q-value in brackets *** significant at the 1%, ** significant at the 5%, and * significant at the 10%.

85
14 excessively dependent on the evolution of oil prices and external shocks, respectively<sup>13</sup> . To avoid variation due to changes in the sample throughout time we include only countries with GDP data for all years in the [-12,9] period. We also exclude countries that have gone through serious conflicts as a large literature documents their pernicious impact on economic growth.<sup>14</sup> The determination of this sample is in line with the methodology applied in Jinjarak et al (forthcoming)<sup>15</sup> .

Finally, we delete the years of economic crisis that surrounded trade reforms, as we observe later that in average our sample countries experience a period of economic downturn four years before reform and a rebound in the following year. Such exclusion is particularly needed for the countries that experienced hyperinflation.

Our sample selection technique also permits a more accurate application of within country estimation of the impact of trade liberalization on other economic indicators, such as investment, exports, share of manufacturing exports, industry value added, and exports concentration. These indicators will allow us to obtain a comprehensive picture of the impact of trade liberalization on economic performance.

The regressions on GDP growth are estimated using the entire sample of 39 countries and also for subgroups of countries grouped by world region, income per capita, and size of the population. We consider non reversed trade liberalization episodes between the years 1970 to 2004 and for each country we analyze economic performance 12 years before to 9 years after trade reforms, excluding the crisis years [–4,1].

> 13 A valid critique to our methodology in this regard is that several other countries that remain in our sample are highly dependent on a handful of non-oil commodities and thus could be highly volatile. Yet, we cannot exclude such countries due to sample size considerations and expect that the inclusion of terms of trade would control for volatility in commodity prices.

> 14 Collier and Hoeffler (1998). We define conflict countries as those that experienced war (internal or external) according to Gleditsch et al. (2002)

> 15 The obvious caveat of concentrating on this sample is its reduced size. Whereas SW and WW use more than 100 countries in their analysis we are left with only 39.
# **5.2 Five Destinations**

The third block of games adds destinations 4 and 5 with wages determined by: (8) 4ii ii 4ii ww = 900 + 100ss + ee (9) 5ii ii 5ii = wwWhere the cost of moving to destination 4 is 50, and to destination 5 is 100; and = 100 + 400ss + 4ee . Note that destination 4 then costs the same to migrate to as destination 2, and always pays a 2ii 3ii 4ii ee = ee = ee wage of 100 less; and destination 5 costs the same to migrate to as destination 3, and always pays 5ii ee a wage of 100 less. The only reason to choose either destination will then be in games with a risk of unemployment, if the risk of being unemployed is lower in one of these destinations, or the unemployment insurance higher.

Figures 4a and 4b show the resulting migration choices across the five locations in each of the nine games. We again see both the scale of migration and the skill selectivity pattern vary across games. The decisions in Games 19 to 22 look similar to those in Games 10 to 13, suggesting that the addition of two irrelevant destinations did not change migration choices. We test this formally in the next sub-section. In Game 23 the unemployment rate in destination 4 is set at 20%, which is lower than the 30% in destination 2, so here we do see switching of destinations compared to Game 14. In Game 24, we see some strategic choices, where some participants choose the lower wage destination 4 instead of 2, believing that less people will move there and so the chance of unemployment will be lower. This increases the overall migration rate in the Lisbon sample in Game 24 to 38.3 percent, compared to 28.6 percent in Game 15. In Nairobi the increase is smaller, from 30.2 percent in Game 15 to 33.2 percent in Game 24.

In Game 25 there are potentially 8 pieces of information individuals can pay to acquire (the unemployment rate and unemployment insurance amount for each of the four destinations). The endowment was set to 100* _s+_ 200 for this game, so that all participants could afford to purchase full information if they wish, and still have enough money left to move to their destination choice. However, only 55 percent in Lisbon and 58 percent in Nairobi purchase any information. Not a single individual in Lisbon purchases full information: the maximum is 5 pieces of information, and the median, conditional on purchasing, is 2 pieces. In contrast, 7.9 percent in Nairobi purchase all 8 pieces of information, and the median conditional on purchasing is 3 pieces of information.

19
# **References**

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- A. Adams-Prassl, T. Boneva, M. Golin, and C. Rauh. Inequality in the impact of the coronavirus shock: Evidence from real time surveys. 2020.

- D. Altig, S. B. Baker, J. M. Barrero, N. Bloom, P. Bunn, S. Chen, S. J. Davis, J. Leather, B. Meyer, E. Mihaylov, P. Mizen, N. Parker, T. Renault, P. Siemtanka, and G. Thwaites. Economic uncertainty before and during the covid-19 pandemic. _Journal of Public Economics_ , Forthcoming, 2020a.

- D. Altig, J. M. Barrero, N. Bloom, S. J. Davis, B. Meyer, and N. Parker. Surveying business uncertainty. _Journal of Econometrics_ , 2020b.

- S. Aum, S. Y. T. Lee, and Y. Shin. Covid-19 doesn’t need lockdowns to destroy jobs: The effect of local outbreaks in korea. Working Paper 27264, National Bureau of Economic Research, 2020.

- S. R. Baker, N. Bloom, S. J. Davis, and S. J. Terry. Covid-induced economic uncertainty. Working Paper 26983, National Bureau of Economic Research, April 2020. URL http://www.nber.org/ papers/w26983.

- D. Balla-Elliott, Z. B. Cullen, E. L. Glaeser, M. Luca, and C. T. Stanton. Business reopening decisions and demand forecasts during the covid-19 pandemic. Working Paper 27362, National Bureau of Economic Research, June 2020. URL http://www.nber.org/papers/w27362.

- A. Balleer, S. Link, M. Menkhoff, and P. Zorn. Demand or Supply? Price Adjustment during the Covid-19 Pandemic. CESifo Working Paper Series 8394, CESifo, 2020. URL https://ideas.repec. org/p/ces/ceswps/_8394.html.

- J. M. Barrero, N. Bloom, and S. Davis. Covid-19 is also a reallocation shock. _Brookings Papers on Economic Activity_ , Forthcoming(July), 2020.

- A. W. Bartik, M. Bertrand, Z. Cullen, E. L. Glaeser, M. Luca, and C. Stanton. The impact of covid-19 on small business outcomes and expectations. _Proceedings of the National Academy of Sciences_ , 117 (30):17656–17666, 2020.

- I. Bartlett, Robert P and A. Morse. Small business survival capabilities and policy effectiveness: Evidence from oakland. Working Paper 27629, National Bureau of Economic Research, July 2020.

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14
suggests that both tariff cuts in PTAs and IPRs reforms, undertaken on a non-discriminatory basis under such agreements, encourage technology transfers to middle-income and emerging economies (Maskus, 2012).

Thus, there may be remaining concerns about endogenous selection. To alleviate the problem, we estimate specifications in which we eliminate from the sample trade with the major partner in each of the treatment agreements, generating estimates of the trade impacts with respect to all other countries, both in the aggregate and bilateral trade. We regard this as the most rigorous specification, in that it extracts the possibility that the intent of the major partner was to increase trade in IP-sensitive goods with treatment countries, including through trade in intermediates, leaving just residual trade effects with third countries.

Our selection of treatment IPAs (and treatment countries as members) is as follows. In case 1 we designate treatment IPAs as those legally enforceable agreements involving the United States, the EU or EFTA as a partner country.<sup>11</sup> This selection is made in part because these are the main _demandeurs_ of elevated IPRs standards. However, we also wish to compare results using the World Bank database with the same specification of IPAs using the DESTA database in Maskus and Ridley (2020). In case 2 we consider all PTAs in which IPRs are designated as legally enforceable and in case 3 we use such PTAs where the United States, EU or EFTA are not partners.<sup>12</sup> In the final two cases we shift from permitting the nature of full agreements to determine the treatment selection to considering, in a basic fashion, whether specific BTRIPS provisions matter for trade sufficiently to serve as meaningful selection devices. We do this in part to explore the explanatory power of the World Bank database in its considerable specificity. However, this focus is of more general interest because of the importance placed on TRIPS-Plus standards by negotiators and the attention they draw in the policy debate. If, for example, American negotiators place heavy emphasis on patent extensions, test-data protection, and anticircumvention of digital copyrights, their inclusion may bear detectable traces in the trade data. In essence, we explore whether IP-related PTAs with specific BTRIPS standards have trade

> 11 To clarify, we select PTAs in which the IPRs are designated as LE. These are agreements labeled WTOX_ipr_le=2 in the World Bank source.

> 12 Appendix Table A1 lists IPAs involving the United States, the EU or EFTA, and all those considered legally enforceable by the World Bank. We exclude the North American Free Trade Agreement (NAFTA) because it was implemented prior to our sample period. Lists of other groupings are available on request.

14
Another drawback is that the combination of GDI per capita with some distributional statistics (to reflect national income distribution) introduces a mixing of two aggregates, calculated from different sources, and this “mixing” is not distributionneutral. On the one hand, we are using as the country GDI per capita, and on the other, we are applying to this mean, distributional parameters obtained from surveys of household disposable income.<sup>13</sup> It was already explained that the two instruments are different by definition. But in addition, such an adjustment is not distribution-neutral. We know that surveys tend to underrepresent capital income or undersurvey rich people (see Mistiaen and Ravallion, 2003).<sup>14</sup> Thus, a simple upscaling of all survey incomes by a given parameter will reduce poverty below what it really is and underestimate inequality.<sup>15</sup> When a different mean (GDI per capita) is applied to a survey-based distribution, we implicitly allocate the difference between GDI per capita and disposable household per capita income across all households (more exactly, in proportion to reported household income). Poor people’s income is increased in the same proportion as rich people’s income. But if most of the difference between the two concepts is due to unreported income of the rich then this approach artificially inflates incomes of the poor.

Now, income of the rich which accounts for the bulk of the difference between GDI and disposable income is of two types: first, the definitionally-different part which consists of publicly-financed health and education, corporate profits etc. that are 13 “The difference in coverage and definition between [National accounts] and survey means that, even if everything were perfectly measured, it would be incorrect to apply inequality or distributional measures, which are derived from surveys which measure one thing, to means which are derived from national accounts, which measure another (Deaton., 2003, p.35).

14 Income from property is notoriously underestimated in household surveys (even leaving aside the fact that most surveys do not include capital gains at all). Concialdi (1997, p. 261) claims that the best available French household surveys underestimate capital incomes by about 40 percent. Wagner and Grabka (1999) estimate German property income to be underestimated by almost one-half compared to National Accounts data. In Japan, according to Ishizaki (1985) only 12 percent of property income is “captured” by household surveys (quoted in Bauer and Mason, 1992, p. 407).

15 We speak of upscaling rather than downscaling because GDI per capita is normally greater than household per capita disposable income.

9