rafmacalaba/datause-encoder-data huggingface dataset:
the same dataset. Estimated program impacts appear to be sensitive to different econometric approaches used. Also, different studies tend to focus on different treatment effect parameters, with some studies estimating average effects of treatment on the treated and other studies focusing on local treatment effects for specific subpopulations. Whether and to what extent microcredit programs help poor individuals is still a matter of intense debate, but we will summarize here some of the accumulated evidence from randomized field studies and nonexperimental studies.

Pitt and Khandker (1998) is an influential and often cited nonexperimental study that estimates the impact of participation in one of three Bangladesh group-based lending programs (the Grameen Bank, Bangladesh Rural Advancement Committee (BRAC), and Bangladesh Rural Development Board (BRDB)) on women‟s and men‟s labor supply, on girls‟ and boys‟ schooling, on expenditures and on assets. It explores how the program impacts vary by gender of the borrower. Very few women work in the regular labor market in Bangladesh, because it is a Islamic society that excludes women from many activities. Self-employment is a viable alternative for these women, because the productive activities can be carried out in their home and while taking care of children.

Pitt and Khandker (1998) estimate the effect of the lending program using survey data collected in 87 rural Bangladeshi villages in 1991-92. In recognition of the fact that the program was nonrandomly placed, their analysis does not simply compare individuals that received and did not receive the program. Rather, they use a feature of the program eligibility rule as a way of generating a comparable comparison group. Only landless households, defined as households with less than one-half acre of land, were eligible to participate in the program; households with more land were ineligible. Their identification strategy estimates conditional household demand equations for households that were and were not eligible to participate in the program by virtue of the land ownership restriction but that lived within the same village (the effects of regional location are controlled using village-level fixed effects). An assumption required to justify this approach is that land ownership is uncorrelated with the unobserved household type. The estimation uses data on villages where the microcredit programs were available as well as villages where the programs were not available. Indicators for program availability within the village essentially serve as instruments for program receipt.

29
the one hand, the crisis is related to the tragic events occurring in 1994, such as the assassinations of two influential political leaders and the peasant uprising in the southern state of Chiapas, which most likely had a negative impact on foreign investors' confidence. On the other hand, the crisis is also a consequence of poor macroeconomic management and a lack of strong fundamentals.

Unfortunately, the effect of the former component is not measurable, at least not at this point in time given economists' current understanding and handling of sociopolitical events. The second component, however, is strongly supported by our previous analysis and by the fact that by end 1993 Mexico had poor fundamentals, at least compared with other countries within the HCIR group. By the end of 1993 all fundamentals were better for the average country within this group than for Mexico, except for the fiscal deficit and total external debt (both as a percentage GNP; table 10). It could be argued, then, that Mexico was more likely than other high-recipient countries to suffer a crisis if a negative shock occurred.

Furthermore, our results also seem to be consistent with the different impact that the "tequila effect" had across regions and among countries within those regions. It is well known that Latin American countries were more affected by the Mexican crisis than East Asian countries, and that within the Latin America region Argentina was the country that suffered the most. These differences can be well explained by noting that: first, among the Latin American countries Argentina, like Mexico, also had poor f-undamentals at the end of 1993-in fact these two countries had the worst fundamentals among all HCIRs (see Table A.2)-and second, in recent years the East Asian region has experienced an investment boom (with the exception of the Philippines) while the Latin American region has experienced a consumption boom (with the exception of Chile; figure 7).32 32 For this comparison across regions see also World Bank (1995: 16-17).

20
<!-- Start of picture text --> Mali 2006, rural areas<br>Women 15-49<br>S oO Married, once<br>= me MViarried, prev. widow<br>= =m Married, prev. div.<br>2 to ||@=m Curr. widow<br>5 ~ |)== Curr. div.<br>Ss ¢<br>o s 4 ate<br>2 . ot; on<br>aetEssee<br>c®o °ue ¥<br>=: ao?o*<br>= oN] = &<br>o O , v6<br>= ’C<br>=?<br>Y= i<br>10 20 30 40 50<br>Age<br><!-- End of picture text -->

<!-- Start of picture text --> Mali 2006, urban areas<br>Women 15-49<br>< co2<br>©<br>=<br>fs -<br>oO -<br>wT Pid<br>(= al<br>oO<br>Qa<br>oO<br>Zo)<br>= + Je ee<br>(=<br>fo}2 >ad<br>= Aad<br>re) N -* --* m= Marr., onceprev. wid.<br>) o% me Marr., prev. div.<br>= of m= Curr. widow<br>dp) o == Curr. div.<br>10 20 30 40 50<br>Age<br><!-- End of picture text -->
**Figure 4.3: Cumulative density of electricity consumption**

<!-- Start of picture text --> 100<br>80<br>60<br>40<br>20<br>0<br>Subsidy threshold (kWh/mo.)<br>Poor customers<br>Non-poor customers<br>50 100 150 200 250 300 350 400 450 500<br> >500<br>households<br>Cumulative percentage of<br><!-- End of picture text --> _Source:_ World Bank calculations using the ENCOVI 2000, Instituto Nacional de Estadística – Guatemala

**<u>Table 4.1: Comparison of electricity consumption</u>**

||Poor|Non-Poor|
|---|---|---|
|Connection rate|46|76|
|Average consumption (kWh/mo.)|48|128|
|Electricity expenditure ($/mo.)|||
|•With social tariff|5.1|14.4|
|•Without social tariff|7.2|21.9|
|Electricity expenditure as percentage of monthly budget|||
|•With social tariff|2.7|2.6|
|•Without social tariff|3.7|4.1|

_Source:_ World Bank calculations using the ENCOVI 2000, Instituto Nacional de Estadística – Guatemala It is important to question who benefits from the current social tariff policy, and in particular how effective is it at protecting the most vulnerable households. Owing to the high level of the consumption threshold, the social tariff evidently benefits a considerable number of households who live above the poverty line. Indeed, about 65% of the beneficiaries of both the old and the new schemes are not poor (errors of inclusion<sup>24</sup> ), and given that their consumption is relatively high they absorb an even larger percentage of the resources devoted to the subsidy (leakage rate<sup>25</sup> ), 90% in all (Figure 4.4). The subsidy reaches 100% of poor households with electricity connections (that is there are no errors of exclusion<sup>26</sup> ), but only 40% of poor households enjoy these connections and hence benefit from the subsidy.

Given that poor households consume substantially less electricity than non-poor households, the costeffectiveness of the social tariff could be significantly improved if the consumption threshold was reduced. In order to explore this possibility, a simulation exercise was performed to calculate the errors of inclusion and exclusion, as well as leakage rates, for a series of different consumption thresholds (Figure 4.4). There is an underlying assumption in this exercise that electricity consumption will remain constant despite the changes in the tariff structure by moving the consumption thresholds. The results show that the targeting performance of the subsidy could be significantly improved with an eligibility threshold of 100 kWh per month. Errors of inclusion would fall from 75% to 65%, and the leakage rate from 90% to 75%. At the same, time errors of exclusion would rise only 0% to 8%, while the overall cost of the subsidy would fall to almost a quarter of its current level, from $48.9 to $13.2 million per year.

> 24 Errors of inclusion are defined as the percentage of subsidy beneficiaries who are not poor. 25 The leakage rate refers to the proportion of the total subsidy expenditure that flows to the non-poor. 26

> Errors of exclusion are defined as the percentage of the poor who are not subsidy beneficiaries.

31
<!-- Start of picture text --> 2010<br>10th percentile<br>employment<br>50th percentile<br>of<br>90th percentile 2005<br>series<br>2000<br>interpolated<br>(b) Services<br>the<br>1995 and<br>1990<br>non-interpolated<br>the<br>2010<br>using<br>10th percentile<br>50th percentile<br>90th percentile estimated<br>2005<br>distortions<br>2000 to<br>(a) Industry<br>correspond<br>1995<br>lines<br>dashed<br>1990 the<br>and<br>solid<br>The respectively.<br>4 3 2 1 0<br>Distortions in Services<br>4 3 2 1 0<br>Distortions in Industry<br><!-- End of picture text --> 25
**TABLE 6: Investment financial performance, GDP per capita, and legal origins.** The dependent variable is the investment-level PME vs. S&P500. The natural log of GDP per capita is measured as a difference from the sample mean of the natural log of GDP per capita on the year of the first cash flow associated with the investment. Country legal origins are as classified by La Porta et al. (1999). The omitted category is French or German legal *** ** * origins. Standard errors are clustered at the country-year. p<0.01, p<0.05, p<0.1

||(1)|(2)|(3)<br>Qua|(4)<br>ntile Regr|(5)<br>ession|(6)|
|---|---|---|---|---|---|---|
||OLS|0.1|0.25|0.5|0.75|0.9|
||PME|PME|PME|PME|PME|PME|
|Panel A) Direct investments,|vintage pr|e-2010|||||
|Ln(GDP per capita)|0.46|0.00|0.05**|0.00|0.00|-0.20|
||(0.36)|(0.02)|(0.02)|(0.04)|(0.08)|(0.29)|
|British legal origins (=1)|-0.39|0.00|0.03|-0.10|-0.02|-0.00|
||(0.47)|(0.04)|(0.04)|(0.09)|(0.19)|(0.60)|
|Socialist legal origins (=1)|1.62|0.02|0.21***|0.30**|0.30**|0.66|
||(1.93)|(0.05)|(0.07)|(0.12)|(0.14)|(1.23)|
|Constant|2.17***|0.00|0.15***|0.69***|1.44***|2.96***|
||(0.45)|(0.02)|(0.02)|(0.05)|(0.09)|(0.23)|
|R-squared|0.0036|0.0025|0.0033|0.0030|0.0027|0.0004|
|Number of observations|1,299|1,299|1,299|1,299|1,299|1,299|
|Panel B) Fund investments, v|intage pre|-2010|||||
|Ln(GDP per capita)|0.57|0.06|0.11*|0.19***|0.20|0.65***|
||(0.37)|(0.05)|(0.06)|(0.07)|(0.12)|(0.15)|
|British legal origins (=1)|1.97|0.13|0.08|0.15|0.18|0.15|
||(1.74)|(0.10)|(0.12)|(0.15)|(0.26)|(0.31)|
|Socialist legal origins (=1)|0.75*|0.10|0.07|0.24|0.48*|2.14***|
||(0.42)|(0.11)|(0.14)|(0.19)|(0.26)|(0.73)|
|Constant|0.56***|0.12*|0.29***|0.56***|0.87***|1.78***|
||(0.20)|(0.07)|(0.07)|(0.09)|(0.12)|(0.24)|
|R-squared|0.0140|0.0092|0.0020|0.0018|0.0013|0.0001|
|Number of observations|152|152|152|152|152|152|
|Country fxed efects|No|No|No|No|No|No|

37
between the duration of treatment and the program effects on consumption of alcohol and tobacco.

## **Level Estimates**

Other studies, while not estimating the impact of transfers on consumption of or expenditures on temptation goods, have sought to quantify how many beneficiaries use transfers for temptation goods, or how much of the transfers has been spent on temptation goods; these studies rely either on surveys or focus groups. We identified 11 such studies, representing programs in 8 countries: 6 in Africa, 1 in Asia, and 1 in the Middle East (Table 9). Four of the studies identified a proportion of beneficiaries or households that spent some or all of the transfer on temptation goods. The median proportion was 1.2%, a tiny fraction of households. Even in the one outlier, Lesotho’s Cash & Food Transfers Pilot Project, where about 6% of beneficiaries admitted to spending some of their transfer on alcohol and cigarettes, the study quotes a recipient as saying that it happens “only in rare and discreet cases.” Two more studies, from Malawi and Zimbabwe, identify the proportion of transfers spent on temptation goods: In both cases, the proportion is under 0.5%. The remaining studies simply report that they found no evidence that households were purchasing temptation goods, except one case that reports a “marginal increase.” This evidence is significantly less convincing than the impact estimates, which look at total expenditures rather than transfer expenditures alone, as transfer and other income are fungible. A household could, for example, use the transfer income entirely for education investments but at the same time decrease spending on education from regular income by ten percent. Then they could use that ten percent of regular income for temptation goods. In the respondent’s view, none of the transfer income would have been used for temptation goods, although clearly the transfer is what enabled the increased expenditures. Despite this caveat, these level estimates are consistent with the finding of insignificant quantities being spent on alcohol and tobacco that was already observed in the more reliable estimates on overall expenditures.

# **Discussion**

In this section we discuss some of the implications and challenges related to this analysis. One principal concern when studying the consumption of goods such as alcohol and tobacco, especially in the context of a program where beneficiaries are encouraged not to use the resources on those goods, is that beneficiaries will report low expenditures on those goods 10
6 approach is a generalization of differences-in-differences (DID), which we employ on panel data covering the 28 countries over the period 1990 to 2004. Like DID, our approach eliminates the confounding effects of unobservables that remain constant over time. But unlike DID our approach relaxes the parallel trends assumption that some regard as the Achilles heel of DID.

The paper is organized as follows. Section 2 outlines the payment reforms in the ECA countries. Most went into the 1990s with a Semashko Soviet-style health system. Many shifted to a social health insurance model, and following this shift began to move away from the line-item budget method of paying hospitals. Some shifted to fee-for-service (FFS). Some moved to DRGs. Some shifted to FFS and then to DRGs. Some ended up making parallel payment reforms in the primary care sector, and some ended up imposing global budgets on hospitals. We take these parallel reforms into account in our empirical analysis. An attraction of our study is that we are able to shed light on the relative merits of all three broad approaches to paying providers (Ellis and Miller 2008): payments based on provider characteristics (lineitem budgets being an example); payments based on service characteristics (FFS being an example); and payments based on patient characteristics (DRGs being an example). Section 3 sets out our hypotheses concerning the impacts of these payment method changes on the outcomes of interest, namely inpatient admissions, average length of stay, the number of beds, the bed occupancy rate, health sector spending, and amenable mortality (i.e. causes where timely and effective medical care can result in a premature death being avoided). Section 4 outlines our methods, including the tests we use to assess the validity of different models. We also outline our test of reverse causality, a concern being that DID models may not adequately account for the possibility that direction of causation runs not from payment reforms to changes in
with at least secondary education. As in Section 3, cells with fewer than 50 respondents are dropped, so the final sample contains 2,264 cells, each with more than 400 respondents on average (median 185). The DHS also includes a question about respondents’ religious beliefs, which is used to obtain the fraction of respondents of Christian religion (any denomination). The geographical coverage is slightly smaller than for education, with a sample of 2,083 cells.<sup>34</sup> Consistent with the literature discussed in Section 1, historical missions are assumed to have had positive effects on both education and prevalence of Christianity.

The first column of table 10 reports results of an estimation of equation (1) on the subsample of cells for which a measure of education from the DHS is available. The coefficient on the mission dummy has similar size and precision to the full-sample results. In relative terms, however, the correlation is smaller, owing to the larger incidence of aid projects in this subsample of cells (50 percent compared to 25 percent in table 3).

Columns 2–4 present results for models with different measures of education: average level, fraction with at least primary education, and fraction with at least secondary education. The coefficients on all three measures of education are positive, significant at the 99 percent level, and large. Inclusion of either measure reduces the size of the coefficient on Mission _ik_ . Secondary education seems to be most important here; it has the largest coefficient, and its inclusion almost halves the mission coefficient. Under the assumption that missionary activities have positive effects on education, the coefficient on Mission _ik_ is a lower bound on the true effect. This lower bound ranges from 60 to 90 percent of the main effect in column 1. This suggests that a heritage of high human capital could be one reason for more aid going to mission areas. However, there seems to be room for other explanations as well, since the coefficient on Mission _ik_ is not reduced to zero.

In column 5, the baseline specification is estimated in the subsample of cells for which a DHS measure of religion is available. Although religion seems to play an independent role in aid allocation, the coefficient on Mission _ik_ does not change when a measure of Christian religion is included in the regression. This means that there is no evidence in the data that Christian favoritism is the mechanism behind the correlation uncovered in Section 2.

> 34The question about religion is not included in all countries for all rounds.

38
The paper contributes to the existing literature on sudden stops in several ways. First, we extend the country and time coverage relative to datasets that have previously been used to analyze related topics. Second, we contribute two methodological improvements, by introducing the use of cluster‐robust standard errors into the analysis of sudden stops and by formally testing the exogeneity of this type of crisis. Thirdly, we provide an analysis of the adjustment path of economic growth after a sudden stop, a new angle of analysis in this context.

The rest of the paper is organized as follows. The next Section II describes the data. Section III lays out the estimation methodology and the set of robustness checks applied to quantify both the likelihood of sudden stops of capital flows and their impact on GDP growth. Section IV reports and interprets the estimation results. The last section concludes the paper.

# **II. Data and Descriptive Statistics**

The analysis relies on a data set of 43 countries, 26 emerging and 17 industrialized, consisting of yearly observations for the period 1993‐2006. This dataset represents an improvement relative to previous studies on related topics by extending both, country coverage and time horizon.<sup>1</sup> Countries are listed in Appendix 1, data sources in Appendix 3.

The sample consists of a heterogeneous group of countries with a wide variance of real per capita income levels and growth rates. While industrial and emerging economies in real terms grew by close to 3 percent on average over the period 1993‐2006, the sample exhibits diverse dynamics. For example, starting from a low level, real per capita income has on average grown fastest in Latvia with a 7 percent annual growth rate over the 14‐ year period under consideration. In comparison, Italy had the weakest growth performance with merely 1 percent annual growth on average.

The focus of this paper is on the causes and consequences of sudden stops of capital flows, therefore the sudden stop variable itself and factors explaining this type of crises are in the center of the following data description. First, we explain the sudden stop variable, and give a brief overview of sudden stop incidences in the sample. Second, we explain the construction of sudden stop drivers and describe them.

We define sudden stops with the help of a dummy variable capturing large and unexpected falls in capital flows. We construct this variable following Calvo et al. (2004), based on monthly data to maximize the chances to detect sudden stops, because annual data might hide the origin of such crises. Capital flow figures are generally unavailable on a monthly basis, therefore we proxy them by netting out the trade balances from the changes in foreign reserves. Sudden stops are then defined as episodes in which the year‐on‐year drop

> 1 The dataset that is usually referred to in this type of analysis is based on Calvo et al. (2004), covering 31 countries from 1993-2001.

3
# **Table 3b.  Trade Flows of Tanzania**

|||Imports|||Exports||
|---|---|---|---|---|---|---|
||USD in|||USD in|||
||<br>billion|% of total|% of supply|<br>billion|% of total|% of output|
|**Business Services**|||||||
|Air Transport|0.0|0.9|50.1|0.0|1.0|47.6|
|Communication|0.0|0.4|7.7|0.0|1.1|16.8|
|Insurance|0.1|1.0|95.3|0.0|0.8|104.0|
|Business Services nec|0.2|3.0|8.3|0.3|7.1|14.4|
|Financial Services nec|0.0|0.6|89.0|0.0|0.2|80.8|
|Transport nec|0.2|3.0|39.7|0.2|4.8|49.1|
|Water Transport|0.0|0.1|26.1|0.0|0.2|2.0|
|**Dixit-Stigliz Goods**|||||||
|Chemicals Mineral and Metal Products|1.3|23.6|58.9|0.8|23.4|54.0|
|Energy and Minerals|0.0|0.3|7.4|0.3|7.6|60.0|
|Food Products|0.4|7.7|13.6|0.5|12.8|15.2|
|Petroleum and Coal Products|0.6|11.9|90.0|0.0|0.0|0.0|
|Other Manufacturing|1.6|29.6|78.6|0.1|2.2|23.2|
|Textile and Apparel|0.3|5.5|51.1|0.1|4.0|45.7|
|Wood and Paper Products|0.1|2.6|51.8|0.0|1.3|31.4|
|**CRTS**|||||||
|Agriculture and Forestry|0.2|2.9|3.0|0.8|22.2|13.9|
|Other Services|0.3|5.1|4.7|0.2|5.0|3.2|
|Trade|0.1|1.7|2.7|0.2|5.8|5.8|
|Utilities|0.0|0.0|0.3|0.0|0.4|1.9|

**Source:** Authors’ calculations based on the GTAP 8.1 data set.

48
# **APPENDIX II: FURTHER RESULTS OF THE REGRESSION ANALYSIS**

**<u>Table II-1 Regression results for the sudden onset events (N=77)</u>**

|Model|Gross<br>savings<br>PV dconsu|Gross<br>disaster<br>savings<br>mption inper|Net<br>savings<br>cent ofper cap|Net<br>disaster<br>savings<br>ita income of|Genuine<br>savings<br>theyear befor|Genuine<br>disaster<br>savings<br>e the event|
|---|---|---|---|---|---|---|
|Constant|0.050|0.096***|0.114***|0.147***|0.127***|0.154***|
||(1.13)|(2.73)|(3.48)|(5.36)|(3.90)|(5.62)|
|Savings measures|0.730***|0.606***|0.689***|0.571***|0.614**|0.561**|
||(3.40)|(3.27)|(3.00)|(2.92)|(2.45)|(2.57)|
|R Square|0.133|0.125|0.107|0.102|0.074|0.081|

Note: Significance at the * 10% level;** 5% level; *** 1% level

**Table II-2  Regression results for the** **<u>slow onset event sample (N=21)</u>**

|Model|Gross<br>savings<br>PV dCon|Gross<br>disaster<br>savings<br>sumption inpe|Net<br>savings<br>r cent ofper c|Net disaster<br>savings<br>apita income of|Genuine<br>savings<br>theyear befor|Genuine<br>disaster<br>savings<br>e the event|
|---|---|---|---|---|---|---|
|Constant|0.097|0.131*|0.156**|0.182***|0.172***|0.204***|
||(1.17)|(1.99)|(2.60)|(3.58)|(3.50)|(4.24)|
|Savings measures|0.577|0.515|0.552|0.537|0.729*|0.494|
||(1.56)|(1.56)|(1.29)|(1.38)|(2.00)|(1.68)|
|R Square|0.113|0.113|0.081|0.091|0.174|0.129|

Note: Significance at the * 10% level;** 5% level; *** 1% level 30