rafmacalaba/datause-encoder-data huggingface dataset:
18 term for internal remittances [(INTREM)(log EXP)] is statistically significant for only the highest level of education: higher/university education. In the same table the interactive term for international remittances [(EXTREM)(log EXP] is positive and significant for secondary education.

The results from equation (13) can be used to calculate marginal budget shares for the three groups of households for each level of education. These marginal budget shares are shown in Table 11. When compared to non-remittance receiving households, households receiving internal and international remittances allocate slightly more of their increments to education on the lower levels of education: preparatory and primary school. However, at the higher levels of education – and especially at the secondary school level – households receiving remittances allocate considerably more of their increments to expenditure on education. At the margin, households receiving internal and international remittances spend 19.6 and 142.4 percent more, respectively, on secondary school education than do non-remittance receiving households. Households receiving international remittances also spend more at the margin on higher/university education than do non-remittance receiving households.<sup>x</sup> The results from Table 11 suggest that remittance-receiving households in Guatemala are spending their increments to expenditure with an eye to the expected differential rates of return to various levels of education. For example, a recent World Bank study on Guatemala (2004: Table 7:3) found that when compared to those with no education, people who had completed primary education received 15 percent more in hourly wages, while those who had completed secondary or university education received 51 or 74 percent more, respectively. Households in Guatemala receiving internal or
transfers from the central government from several national sources and documents (listed in the Appendix).

# **4. Empirical Evidence**

This section provides empirical evidence for our theoretical argument from Section 2. We map the theory into the following three empirical tests. First, a key element of our argument is that legislative malapportionment can provide the pre-democratic elite with political influence after transition to democracy. In particular, the historical examples in Section 2 suggest that the predemocratic elite can deliberately allocate lower house representatives to over-represent electoral districts that are aligned with the elite. If this is indeed the case, we should observe that overrepresented electoral districts are more likely vote for parties associated with the predemocratic regime. Section 4.1 empirically examines the correlation between a district’s level of representation and vote shares for parties that are close to non-democratic regimes in six Latin American countries.

Second, Section 2 argues that the fact that malapportionment can preserve some of the pre-democratic elite’s political power may make transition to democracy more likely (since the elite feels less threatened by a democracy and is more likely to agree to a transition to democracy). We investigate this mechanism in Section 4.2, by studying the cross-country, crosstime relationship between malapportionment, transition to democracy, and democratic consolidation.

Third, Section 2 suggests that overrepresented electoral districts may be characterized by a lower degree of political competition and may receive larger transfers from the central government, both of which may help to explain the persistence of the elite’s political power after a transition to democracy. We test whether overrepresented districts are subject to less political competition in Section 4.3 and whether they receive higher transfers from the central government in Section 4.4.

# **4.1 Malapportionment and Political Representation of Pre-democracy Elites**

This section examines whether, in line with the theoretical argument and historical evidence in Section 2, regions in Latin America that have a larger share of representatives in the lower house 11
# 1. Introduction

While much has been written on the relationship between geographical location and objective measures of consumption and welfare (e.g. Elbers, Lanjouw & Lanjouw 2003, Jalan & Ravallion 2002, Ravallion & Jalan 1996, Ravallion & Jalan 1999, Ravallion & Wodon 1999), little is known on how isolation a ff ects subjective welfare. The traditional literature on labor migration has often assumed that rural dwellers prefer living in the countryside and would have to be compensated for migrating to town. This assumption, for instance, underlies original contributions by Lewis (1954) and Harris & Todaro (1970). More recently, Murphy, Shleifer & Vishny (1989) make a similar assumption regarding wage work. Little hard evidence however exists on the utility cost or bene fi t of rural living.

This paper revisits the question of the relationship between isolation and subjective welfare and estimates the welfare cost of geographic isolation. To this e ff ect, we use answers to subjective questions about consumption and income adequacy to test whether utility is equalized across space and, if it is not, whether utility is higher or lower in isolated areas. This approach enables us to investigate in a direct and straightforward manner the question of the relationship between isolation and utility without requiring any assumption about spatial mobility.

The starting point of our empirical speci fi cation is a standard utility maximization model in which isolation is related to utility through its e ff ect on incomes and prices, on the availability of goods and services, and on public goods and externalities. For our empirical investigation, we use a large-scale living standard measurement survey, the Nepal Living Standard Survey (NLSS) of 1995/96. Nepal is the perfect country to study isolation because so much of the country remains inaccessible by road. The NLSS includes a number of questions on subjective consumption and income adequacy. The head of each surveyed household was asked to rank the household’s total income as ‘not adequate’, ‘adequate’ or ‘more than adequate’. Similar questions were asked
underestimate the standard clustered estimates of uncertainty. Estimates of uncertainty based on clustered standard errors cannot be trusted in this setting.

A second striking funding is the large reduction of uncertainty for in-sample municipalities when using the household-level model. The mean MSE is substantially lower for the household model, at just 55 percent and 35 percent as large as the MSE for the sub-area and area-level models, respectively. The median coefficient of variation of the household model estimates is 19.8, which is well below that of the sub-area and area-level models (32.1 and 28.1, respectively). As noted below, the mean squared error and coefficient of variation in the household model is moderately underestimated. If the mean squared error is inflated by a constant to achieve an 86 percent coverage rate, however, the median CV of the household model rises to 25, remaining well below the sub-area and area-level models.

A third striking finding from Table 2 is the difference in precision between the estimates for sampled and non-sampled municipalities. For example, in the household-level model, the median CV rises from 19.7 in the sampled municipalities to 33.4 in the non-sampled municipalities, though this is still below the 38.5 median CV for (in-sample) direct survey estimates using the HorvitzThompson approximation. Since the sampling strategy for the MCS-ENIGH is partly based on population, one possible explanation is that the smallest municipalities are less represented in the survey but are also systematically different from larger municipalities. The fact that the true poverty rate for out-of-sample municipalities is substantially higher than for in-sample municipalities is consistent with this.

A final notable finding is that the gain in precision from utilizing a household model, rather than sub-area or area-level model, decreases substantially when considering out-of-sample municipalities. The greater precision of the household model for in-sample estimates, compared with the sub-area and area-level model, may reflect the ability of the household model to better distinguish between near-poor and wealthy households, because it is modeling welfare levels. This advantage does not apply when predicting out-of-sample, because the estimates are purely synthetic predictions that are not conditioned on the sample data. This may also explain why the 22
1 billion people. Below we describe in detail how we construct our relative size measures, and, provide an example of the variation we exploit in our estimation by tracing out the China shock to the WTO through the relative population and income of countries’ international markets.

Figure 4 displays these variables, averaged in each year for the world and within continents, where observations are weighted by the population of each country. The figure allows us to see how the relative size of the international integrated market in each region changes over time. Each line is a population weighted average of the relative market size, in that year. A number of observations stand out. First, Africa was an early integrator, with many of its largest economies joining GATT early on, for instance South Africa (June 13, 1948), Nigeria (November 18, 1960) and Kenya (February 5, 1964). For a period between the 1970s and 1990s it had the largest relative market size in terms of population. Second, Africa, Asia, and to a lesser extent South America have both integrated with significantly richer countries. Until the 2000s, Africa experienced rapid growth in the market size to which it was linked, as more rich countries joined trade agreements such as GATT. Then, in 2001, when China enters the WTO, relative income falls. Countries in Africa, and other continents, no longer had simply open markets with rich buyers, but a rival in their income bracket. This change in countries’ income-based international market size may have had important implications for development—a point also made in a recent paper by Atkin, Costinot, and Fukui (2021), who argue that China’s entry in world markets pushed many countries, especially in Africa, towards the bottom of the development ladder. Chiquiar and Tobal (2019) similarly show that Mexico reallocated production away from skilled production and towards unskilled production as China’s comparative advantage in skilled production emerged post 2001. Third, countries’ own per-capita GDP and population growth affect the relative size of the market. This can be seen clearly in Asia, where the relative market size in terms of GDP per capita declines over the 2000s, as China gets richer. It is also possible to see how the relative population of Africa’s international market declines in the 2000s, as Africa’s population grows faster than the rest of the world’s.

**Variable profit** We use existing data sets to measure the components of variable profit. To calculate export growth, the first determinant of variable profit, we use the Penn World Tables 9.1 export series (Feenstra, Inklaar, and Timmer, 2015). For total factor productivity growth in agriculture, the second determinant of variable profit, we use the international agricultural productivity series of the United States Department of Agriculture’s Economic Research Service (Fuglie, Wang, Ball, et al., 2012).

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speed. Comparing firms with cases before and after the reform, we find improvements in firms’ perception of the justice system. Taken together, these results support the notion that firms involved in court cases after the introduction of the reform experienced net positive economic gains, bringing new case-firm-level evidence to the literature on the costs of procedural delays (Alencar & Ponticelli, 2016; Djankov et al., 2010, 2020; Lilienfeld-Toal et al., 2012).

# **2 Civil and commercial justice in Senegal**

Senegal’s civil and commercial legal procedure is associated with a high degree of formalism and low legal efficiency (Djankov et al., 2003). Senegal ranked 166 out of 185 economies in the contract enforcement category of the 2013 Doing Business Report, suggesting the speed of commercial dispute resolution could be significantly improved (Doing Business, 2013).<sup>2</sup> Yearly, the Regional First Instance Court of Dakar adjudicates a dispute amount equivalent to 3–6% of Senegal’s GDP. As this capital is stuck in lengthy litigation, it is easy to infer large economic costs (Barro, 1991; Mankiw et al., 1992). We now detail the architecture of the court and legal procedure.

In the Regional First Instance Court of Dakar, judges are organized in chambers, consisting of a president and two additional judges. While the court adjudicates all types of affairs, we focus on civil and commercial justice. At the time of the reform we study, there were four commercial chambers and two civil chambers in the Court. Tables 1 and 2 describe the variation in caseload size and characteristics we have access to at the chamber and case

> 2The Doing Business Report’s enforcing contracts indicator collects its data through a standardized case study with a pre-defined claim value and very specific assumptions. Among such assumptions is that the case is disputed on the merits and that an expert is appointed. The Doing Business Report’s trial and judgment indicator includes pre-trial and decision proceedings, as well as the time to obtain a written judgment and the period within which any party can appeal the first instance decision. In 2014, the Doing Business Report indicated a 420-day duration for trial and judgment. Upon request from the Ministry of Finance of Senegal, and on the basis of the present analysis of Decree n<sup>_◦_</sup> 2013-1071 combined with its own methodology, the Doing Business team adjusted this figure down to 390 days in the 2018 report (and adjusted the duration down retroactively going back to 2015).

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The yield curve utilized in the MWR computations was the average of the daily yield curves in March of each of those five years.<sup>7</sup> The second technical limitation that had to be addressed was the absence of debt instruments with sufficiently long duration. Although Chile has had more success in lengthening the maturities of debt instruments than most other emerging countries, the yield curve still does not cover the possible life of annuity payments. Consistent with the approach taken by James, Iglesias, and Martinez (2005), the yield curve was assumed to be flat after 20 years. This solution seems reasonable, as the yield curve in the months examined is essentially flat in the durations from 15 to 20 years. Finally, the alternative discount rate was constructed by adding the actual spread of corporate bonds over the PRC-20 for each of the periods 2002 - 2004. In March of 2002, 2003 and 2004, these spreads were 1.7, 2.5 and 1.4 percent, respectively.

# **4. The Data**

Most empirical studies generally involve the collection of several annuity quotations, the computation of averages for different categories, and the calculation of MWRs for these categories (e.g., single annuities by sex and age, joint annuities, guaranteed annuities). The high level of disclosure in Chile includes information on every individual annuity sold. As a result, it is possible to compute MWRs for all these categories using actual sales.

The access to actual annuity sales represents a significant improvement over other studies, because the computed MWRs are more consistent with the value actually provided to customers. Another advantage of the study is the much larger size of the sample and the wider range of data points generated. This allows more robust estimates of the averages of different categories, the econometric analysis of some of the main determinants of MWRs, and a more robust analysis of dispersion of annuity prices and transparency of the annuities market.

At the same time, it is important to recognize the possible problems of comparability with other studies. The use of actual annuity sales may lead to higher MWRs than those computed with quotations, even in cases where there are no real differences. This is because customers receive a number of quotes and typically exercise preference for one of the better quotes. Therefore, data based on actual annuity sales will typically capture the better quotes, while data based on quotations will typically reflect the average of several quotes. As a result, MWRs produced with actual sales will tend to be higher.<sup>8</sup> The much larger sample used in this study may also be a source of differences. If the quotations collected in other studies are not representative of the universe of annuity sales, the results and comparisons may be biased.

> 7 The authors are grateful to the assistance provided by Messrs. Klaus Schmidt-Hebel and Jorge Perez, of the Central Bank of Chile.  The Central Bank adjustments result in higher yields than those generated by the direct application of the RiskAmerica software.

> 8 This problem is recognized by Cannon and Tonks (2004).
8 in HICs), we obtain the shock for women only (e.g., 8.3*1.15 = 9.5% in HICs). Lastly, knowing the female share in the labor force before the shock, we estimate the shock for men only (e.g., 7.2% in HICs). See Table 2 for the resulting values.

# **H Robustness for the Analysis by Gender**

**Important Events FE.** Since we focus on workers aged 18-67 in samples from 1990-2016, we study individuals born between 1923 and 1998. For this approach, we thus construct for each country periods based on important years, e.g. for the U.S., 1923-1928, 19291932, 1933-1940, 1941-1944, 1945-1953, 1954-1961, 1962-1963, 1964-1967, 1968-1973, 1974-1979, 1980-1989, 1990-1993 and 1994-2000, due to important events in 1929 (Great Depression), 1933 (New Deal), 1941 (Pearl Harbor), 1945 (World War II ends), 1954 (ends of racial segregation in schools), 1962 (Cuban Missile Crisis), 1964 (Civil Rights Act), 1968 (Martin Luther King assassinated), 1974 (Watergate), 1980 (Reagan), 1990 (Gulf War starts, Cold War ends), 1994 (Nafta), 2001 (9-11), and 2007 (Great Recession). For Kenya, we use 1920 (Crown Colony), 1940 (Italian attack), 1944 (Kenyan African Union), 1947 (Kenyatta becomes KAU leader), 1952 (Mau Mau rebellion), 1956 (rebellion ends), 1960 (state of emergency ends), 1963 (Independence), 1969 (Mboya assassinated), 1978 (Kenyatta dies, rule of Moi), 1982 (one-party state), 1987 (opposition suppressed), 1992 (elections, conflict), 1996 (constitution amended), 2002 (Moi’s reign ends), 2007 (electoral violence), 2010 (constitution, East African market), 2013 (terrorist attacks).

We identify these important events using information from standard sources such as Wikipedia. For each country, we read the top of the Wikipedia webpage of the country (in English as well as in the main language of the country) as well as the “contemporary/modern period” and “colonial period” sections.<sup>9</sup> We cross-check this information using other sources, e.g. the BBC Profile of each country.<sup>10</sup> We then include in the regressions estimating the returns country-specific period dummies equal to one if the individual was aged between 18 and 67 during the period(s), for countries with at least two years of data. Doing so captures the fact that each person was affected by multiple events during her lifetime. For example, an American person born in 1931 was 18 in 1949 and 67 in 1998. For her, the 1945-1953, 1954-1961, ..., 1990-1993 and 19942000 period dummies are equal to one. Of course, blindly following Wikipedia-BBC may lead us to include events that might not be that “important” for workers. At the same time, it is better if we blindly follow their selection of important events rather than us cherry-picking the events ourselves. Selecting too many events by including events that might not appear so “important” should also lead to more conservative estimates because the included cohort fixed effects are then more refined, i.e. lump together fewer

> 9See https://en.wikipedia.org/wiki/United ~~S~~ tates for the U.S. Accessed 03-15-2019. 10See https://www.bbc.com/news/world-us-canada-16761057 for the U.S. Accessed 03-15-2019.
data from the final follow-up survey in 2010 (Round 3). We focus on the program effect on the treated households (ATE) and estimate the following regression:

# (1)

where _yihv_ is an educational outcome for child _i_ in household _h_ and village _v_ in Round 3 _, CCThv_ is the treatment indicator that takes the value one if a child lives in a household that was randomly selected to receive conditional cash transfers and zero otherwise, _UCThv_ is the treatment indicator that takes the value one if a child lives in a household that was randomly selected to receive unconditional cash transfers and zero otherwise, _Xihv_ is a vector of child characteristics (gender and age) included to reduce residual variation across arms after randomization, and ε _ihv_ is a random, idiosyncratic error term.

Since our data collection included baseline and follow-up surveys, we can control for differences across villages in the baseline values of the variables. To do so, we use the following difference-in-differences model: (2) where _yihvt_ is an educational outcome for child _i_ in household _h_ in village _v_ and year _t, T2_ and _T3_ are round indicators for the first and second follow-up surveys (Rounds 2 and 3, respectively), _Dj_ is the treatment indicator that takes the value one if a child lives in a household that was randomly selected to receive treatment _j_ (CCT or UCT) and zero otherwise, _Xihvt_ is a vector of child characteristics (gender and age), _Lν_ is a village fixed effect, and ε _ihvt_ is a random, idiosyncratic error term.<sup>22</sup> The impact of transfer scheme _j_ ( _j_ =1, 2) in period _t_ (t=2, 3) is given by _α t j_ , the coefficient of the interaction between the treatment status and the round dummy. Since

> 22 Correlation among the error terms of children living in a village and experiencing similar shocks in the baseline or follow-up rounds, combined with the design effect of our village-level before and after treatment, might bias the OLS standard errors downward, so in all regressions we cluster the standard errors at the village*follow-up level.

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