rafmacalaba/datause-encoder-data huggingface dataset:
baseline, the women who self-select into our sample are poorer than the average rural Ugandan household.<sup>5</sup> Upon graduating from the program, treated women are 16pp more likely to have an active business than women in the control group. They own 0.22 more businesses, on average, at endline. The program is also effective at promoting productive entrepreneurship: treated women are 10pp more likely to generate positive profits (off a control mean of 59%) and they are 8pp more likely to have positive profits in additional businesses (off a control mean of 16%). Although individual effects on profit levels in both the main business and all other businesses are noisy, our index of intensive-margin business performance shows positive, significant effects at both midline and endline. Importantly, our effects represent gains in women’s employment, not simply switching between salaried and self-employment: treated women are 8pp more likely to be employed at midline (over a control mean of 72% of women being either employed or self-employed).

We exploit the unanticipated market shock of the first COVID-19 lockdown in Uganda to test for women’s ability to cope with negative economic shocks. High-frequency SMS data shows that the program is highly effective at enabling women to navigate the first COVID lockdown. Treated women experience no decrease in revenues relative to the period immediately preceding the lockdown. By contrast, the control group only recovers to pre-lockdown revenue levels a month before the lockdown was fully lifted. We interpret this as promising evidence that skills-based programs can increase women’s economic resilience.

We examine dynamic treatment effects on savings, investments, and household consumption spending to understand how women allocate their earnings. We find no significant effects on savings or investments at midline, right after program completion. However, treated women invest 97% more in other businesses at endline and our index of savings and investment outcomes shows positive, significant effects. Together, results on savings and investments indi-

> 5Half of the sampled women have an active business at baseline, and merely 11% are employed outside of self-employment. Many existing businesses are in perishable goods, livestock, and energy, but we also observe service-based businesses like salons as well as restaurants, retail, and construction.

5
**Table 4: By age**

||**Belo**|**w Median A**|**ge (27) Wo**|**men**|**A**<br>|**bove Media**<br>|**n Age Wom**<br>|**en**<br>|
|---|---|---|---|---|---|---|---|---|
||**1**|**2**|**2**|**4**|**5**|**6**|**7**|**8**|
|Reform* Non-<br>homework|0.154**<br>(2.02)||||0.082<br> (1.01)||||
|Reform* Paid-<br>work||0.177*<br>(1.84)||||0.112<br>(1.23)|||
|Reform* All-<br>year-work|||0.242*<br>(1.76)||||0.036<br>(0.19)||
|Reform*Educati<br>on||||0.009*<br>(1.91)||||0.002<br>(0.31)|
|Constant|0.231***<br>(8.66)|0.234***<br>(9.2)|0.227***<br> (7.91)|0.200***<br>(5.52)|0.471***<br>(11.61)|0.473***<br>(11.89)|0.473***<br>(11.86)|0.479***<br>(15.46)|
|N|172|172|172|172|172|172|172|172|
|R sq.|0.45|0.44|0.45|0.45|0.55|0.55|0.55|0.55|

The result from estimating equation 1 for all occupations, all geographic areas. The dependent variable is women share in occupation and t-stats are in parentheses. Occupation share in the geographic area, the geographic area-time and occupation dummies were controlled for but omitted from table. Standard errors are clustered at the level of the geographic areas

***significant at 1%, **significant at 5%, *significant at 10%.

# **Table** **<u>5: By marital status</u>**

|||**Married**<br>|**Women**<br>|||**Single**<br>|**Women**<br>||
|---|---|---|---|---|---|---|---|---|
||**1**|**2**|**3**|**4**|**5**|**6**|**7**|**8**|
|Reform* Non-<br>homework|0.040<br>(0.56)||||0.145**<br>(2.11)||||
|Reform* Paid-<br>work||0.166**<br>(2.04)||||0.126*<br>(1.77)|||
|Reform* All-year-<br>work|||-0.068<br>(-0.47)||||0.252*<br>(1.95)||
|Reform*Education||||-0.001<br>(-0.16)||||0.009**<br>(2.18)|
|Constant|0.409***<br>(12.49)|0.407***<br>(12.76)|0.414***<br> (11.88)|0.467***<br>(8.95)|0.081***<br>(3.2)|0.085***<br>(3.56)|0.076**<br>(2.77)|-0.021<br>(-0.74)|
|N|172|172|172|172|172|172|172|172|
|R sq.|0.48|0.48|0.48|0.48|0.45|0.44|0.45|0.45|

The result from estimating equation 1 for all occupations, all geographic areas. T-stats are in parentheses. The dependent variable is women share in occupation. Occupation share in the geographic area, the geographic area-time and occupation dummies were controlled for but omitted from table. Standard errors are clustered at the level of the geographic areas.

***significant at 1%, **significant at 5%, *significant at 10%.

24
21 Table 8 * Probit Estimates of the determinants of UnerWLoyment - Mates

|Variable|St<br>|andard Defini<br>of UnemLoymen|tion<br>t|Alt<br>|ernative Defi<br>of UnempLoym|nition<br>ent|
|---|---|---|---|---|---|---|
|YrsSchooL|.013<br>(4.5)|.013<br>(4.2)|.044<br>(3.5)|-.015<br>(-6.3)|-<br>.015<br>(-6.1)|-. 023<br>(-2.7)|
|Yrs School<br>2|||-.001<br>(-2.2)|||.0009<br>(2.1)|
|Age|.021<br>(-17.9)|-.008<br>(-5.9)|-.033<br>(-5.3)|-.028<br>(-32.2)|-.011<br>(-10.8)|-.064<br>-14.4)|
|Age<sup>2</sup>|||.0003<br>(4.3)|||.0007<br>(12.4)|
|Married||.542<br>(-16.3)|-. 496<br>(-14.0)||-. 732<br>(-27.5)|-. 63<br>(-22.4)|
|Cohab.||-.478<br>(-6.4)|-. 425<br>(-5.6)||-.678<br>(-11.7)|-.57<br>(-9.7)|
|North||.006<br>(.23)|.005<br>(.21)||.025<br>(1.18)|.031<br>(1.4)|
|DF||.268<br>(6.42)|.267<br>(6.4)||.179<br>(5.06)|.190<br>(5.3)|
|No. Obs.|43633|43633|43633|45076|45076|45076|
|Means:<br>Unemp.<br>Yrs. Sch.<br>Age<br>Married<br>Cohab.<br>Norrth<br>OF|.03<br>8.1<br>33.4<br>.58<br>.05<br>.41<br>.08|_||.06<br>8.1<br>33.2<br>.57<br>.05<br>.41<br>.08|||

Notes: T-statistics in parentheses. Yrs School = number of completed years of schooling. Unemp = dummy vari'.,Le which takes on the vaLue 1 if individual is unerployed. Married/Cohab = du.r/ variables which take on the vaLue 1 if individual is married or cohabitating with partner. North/OF = dummy variabtrs which take on the vaLue 1 if individual resides in the Distrito Federal (Mexico City) or in one of the Northern states.
students from low-income families. Friedman’s model, on the other hand, is very deregulated and does not include any compensatory element.

By making consumers more aware of the costs of education and by making providers more responsive to consumers’ wishes, there is a belief that this will bring parties closer to a situation in which marginal costs equal marginal benefits. By conditioning the amount of the voucher on the type of education pursued and characteristics of the student, voucher schemes can in principle also take externalities and equity considerations into account.

The effectiveness of vouchers in primary education is intensively studied and debated in the United States. A first wave of studies is based on experiments in Milwaukee and Cleveland. As Carnoy (2001) observes, however, these studies suffer from the fact that vouchers were generally undersubscribed and that those applicants who did not receive vouchers were not necessarily randomly rejected nor carefully followed up. Consequently, it is unclear to what extent the results of these studies report the true causal effect of these studies and to what extent results can be generalized to the population at large. For instance, it is found that parents who received vouchers are more satisfied with the schools their children attend than parents in the comparison group. This finding can, however, easily be attributed by the fact that parents who actively seek vouchers are more dissatisfied initially than others with public schools (as, for instance, in Rouse 1998).

The second wave of studies in the United States is based on experiments conducted in Dayton, Ohio; Washington, D.C. and New York City. Evaluation studies by Howell and 12
# **Appendix Table A5: Self-reported reasons for not adopting more business practices**

|Fraction of firms mentioning this reaso|Control<br>n at follow-up (mu|Treatment<br>ltiple mention)|
|---|---|---|
|Lack of time|0.434|0.408|
|Difficulty of finding skilled workers|0.301|0.265|
|I am happy with my choices|0.294|0.205**|
|Lack of funds|0.294|0.367|
|Owner's cautiousness|0.191|0.229|
|Lack of management support services|0.154|0.117|
|Owner's lack of technical knowledge|0.14|0.112|
|N|136|547|

Notes: This table shows reasons that firms reported on the follow-up survey for not adopting more business practices. These reasons were collected for all firms that participated in the follow-up survey. Stars refer to differences in fractions of the treatment group and the control group. ***, **, and * indicate significance at the 1, 5, and 10 percent level.

26
poverty estimates. Those standard errors are important since they help assess how far the information can be disaggregated (the smaller the area and the number of observation are, the larger the standard errors of the poverty measures are likely to be).

For Guinea, our poverty map is based on the latest Population and Housing Census conducted in 1996 and the second round of the Household Income and Expenditure Survey (EIBEP in French) implemented in 2002/03. While we have an interval of six years between the two surveys, this was not a period of dramatic change in conditions of living in the country, so that we are confident that the two data sources can indeed be compared and used jointly. The questionnaire of the Census is relatively detailed but does not contain information on household incomes or expenditures. At the individual level, the questionnaire covers demographic variables, as well as the education of household members and their economic activities. At the household level, dwelling characteristics are well covered. The Census includes data on 7.2 million individuals living in slightly more than one million households. The field work was done in 5127 enumeration areas (EAs) of about 200 households each on average. As for the EIBEP survey, apart from a wide range of individual and household characteristics, it includes detailed consumption data that have been used to construct the welfare index (expenditure per capita) used in our regression models. Our poverty estimates were derived jointly with government staff from the national Statistical Office, which ensures consistency between the official poverty profile of the country and our poverty map.

The administrative structure of Guinea is simple. The top tier is composed of 8 regions broken down into 34 prefectures. Those prefectures are further dissagregated into communes (sometimes called sous-prefecture). Table 1 presents descriptive statistics on the size of those different administrative levels. There are 341 communes in the census with a 5
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46
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stratified survey. Both the intercept and snowball also overestimate the proportion of adults 18 and over who have worked in Japan, compared to the stratified survey.

Secondly, in accordance with the second hypothesis, we see that weighting the intercept sample does bring it closer to the stratified sample, in terms of links to the Nikkei community. This is the case in both the São Paulo and Parana surveys. There is also some support for the third hypothesis. The snowball survey picks up more second-generation and less third-generation Nikkei than the stratified survey. The intercept survey in São Paulo does get the same proportion of adults by generation as the stratified survey. However, in Parana, where the intercept survey visited less locations, the intercept survey actually oversamples second-generation relative to third generation, and does undersample fourth generation.

**Table 11: Comparison of Characteristics of Nikkei Across Different Sampling Methods**

||Stratified<br>Survey|Unweighted <br>Intercept<br>Sa|Weighted<br>Intercept<br>o Paulo|Snowball|Stratified<br>Survey|Unweighted<br>Intercept<br>Parana|Weighted<br>Intercept|
|---|---|---|---|---|---|---|---|
|**Household Characteristics**||||||||
|Household Size|3.25|3.29|3.45|3.66*|3.32|3.42|3.38|
|_Percentage of households with member who:_||||||||
|Reads Japanese/Nikkei newspapers|13|39***|28***|45***<sup>, +++</sup>|12|21***|18**|
|Listens to Japanese/Nikkei radio programs|8|25***|21***|17*|7|17***|15***|
|Watches Japanese/Nikkei TV programs|23|43***|36**|54***<br>, +++|25|47***|45***|
|Reads Japanese/Nikkei books/magazines|15|42***|30***|52***<br>, +++|16|37***|32***|
|Reads newspapers from Nikkei associations|12|39***|28***|63***<sup>, +++</sup>|9|46***|37***|
|Checks Japanese/Nikkei websites on the internet|5|24***|18***|25***|8|29***|24***|
|**Characteristics of Adults 18 and over**||||||||
|Mean Age|47.2|46.6|45.0|49.2<br>++|43.6|48.0***|48.4***|
|Percentage:||||||||
|Female|52|50|46|56<br>++|51|40**|40**|
|Married|51|48|43|59<sup>+++</sup>|57|60|62|
|Issei|14|15|12|14|8|11|10|
|Nissei|50|47|45|54<br>++|38|53***|56***|
|Sansei|33|36|42|30<sup>+++</sup>|45|35**|32***|
|Yonsei|3|2|2|3|5|1**|1**|
|Have worked in Japan|21|45***|36***|32**|25|34**|34**|
|Sample Size(households/individuals)|204/270|516/516|516/516|100/220|199/330|392/392|392/392|

*, **, and *** denotes that the mean or proportion is significantly different from that in the stratified sample at the 10%, 5% and 1% significance levels respectively.

+, ++, and +++ denotes that the snowball mean or proportion is significantly different from the weighted intercept at the 10%, 5% and 1% significance levels respectively.

Stratified sample individual characteristics are only given for individuals surveyed with the long questionnaire.

31

-  -
estimates we calculate standard errors clustered by village. In Ahmednager, there are 60 surveyed villages, which exceeds Cameron et al.’s (2008) threshold of 50 clusters for reliable standard errors. However, our sample is small if _villages_ are thought of as the independent unit of observation. An outlier village could have an outsized effect on our results (Deaton, 2012).<sup>14</sup> To verify our results, we collapse our data into 60 observations (for example, the change in mean height in each village) and perform non-parametric statistical significance – tests in particular, tests based on rank of observations, and not absolute magnitude. Additionally, we replicate our main result omitting each village in turn.

# **2.4.2 Effects on the clean village prize**

As part of its Total Sanitation Campaign, the Indian government awards villages a Nirmal — — Gram Puraskar Hindi for Clean Village Prize in recognition for becoming open defecation free. Villages certified by government auditors to be open defecation free receive a trophy and a cash prize, presented to the village chairman at a prestigious ceremony in the state or national capital. Although only about 4 percent of all Indian villages have won the prize, this number is much larger in Maharashtra, where over 9,000 prizes have been won, more than any other state and, indeed, about one-third of the total number of prizes awarded. For more information on the Clean Village Prize, please see Spears (2012a).

We treat receipt of the Clean Village Prize as measure of village sanitation coverage that is independent of our data collection, if coarse and noisy. We obtained administrative records from the Indian central government on which villages in Ahmednagar had ever won the clean village prize. Prizes were first awarded to any of the villages we study in 2006. Through the summer of 2012, 12 of the 60 villages studied have won the prize. We will use regression, Mann-Whitney, and Fisher exact statistical significance tests to investigate whether villages assigned to the treatment group were more likely to go on to win this sanitation prize.

> 14For example, we could estimate a large average effect merely because one village where the potential program effect was large happened to be in the treatment group rather than the control group.

13
1

# **Introduction**

A number of studies evaluate the impacts of decentralization on economic growth and public sector size (Davoodi and Zou, 1998; Akai and Sakata, 2002; Oates, 1985; Ehdaie, 1994; and Jin and Zou, 2002). Most of them use the _Government Finance Statistics_ (GFS) of the International Monetary Fund to measure decentralization (the only crosscountry data available then). Unfortunately, GFS indicators do not include information on the level of autonomy of subnational governments in terms of their revenues or expenditures, which is important information when analyzing decentralization.

The OECD has recently published surveys on the fiscal design of 10 European transition countries (OECD 2001, 2002). OECD data allow users to compute indicators of fiscal decentralization that take into consideration the fiscal autonomy of subnational governments. It is then possible to evaluate whether fiscal autonomy affects the relation between decentralization and economic outcomes. Ebel and Yilmaz (2002) use part of this information (2001) to illustrate how previous estimation results could be sensitive to the choice of fiscal decentralization indicator.

This paper uses the combined 2001 and 2002 publications of the OECD. Part I examines the definition of fiscal decentralization and the existing empirical work dealing with its effects on growth and public sector size. Part II introduces the data of the OECD surveys, as well as the decentralization indicators, and the regression models. Finally, part III presents the results.
Impact evaluation does not escape this general trade-off between breadth and identification, but typically locates at the ―narrow‖ end of the spectrum since it identifies changes in performance measures that are directly attributable to the project. For instance, when evaluating a customs modernization program, the performance measure is likely to be something like container dwell time, even though less quantifiable dimensions of customs performance, like security at the borders, may also matter.

But identifying and documenting the chain of causality from program to ultimate outcomes can be challenging for some trade interventions. In trade facilitation programs, it is not always clear what are the micro-level mechanisms by which transport costs reductions influence firms and households and, more generally, economic activity.

In addition, the use of IE can affect incentives in the long run. The focus on narrow, immediate performance outcomes may well lead to measurement biases or, even worse, create perverse incentives when used for monitoring and evaluation. For one thing, it can focus attention on readily measured outcomes at the expense of less easily measured ones. Consider a customs modernization program. Using IE results to design reward schemes for customs officials might lead to over-emphasis on easy-to-measure reductions in clearance times, at the expense of the monitoring of suspect shipments. If, say, there is a low rate of smuggling illicit products, it may take time before the consequences of reduced monitoring get noticed — too long to show up in an IE.

# **5.2 How do we obtain the data?**

The feasibility of rigorous impact evaluation hinges critically on data availability. Whether the IE is based on experimental (RCTs) or quasi-experimental design, it needs to include a baseline survey and at least one follow-up survey. If quasi-experimental methods are used, the baseline survey must include a rich set of covariates to estimate a (first-stage) selection regression. One of the advantages of RCTs, especially in developing countries, is that they are less demanding in terms of data; however, even with randomization, firm-level covariates can be useful in verifying that the treatment and control groups are comparable in their observable characteristics. This is especially important for small samples. The availability of a rich set of covariates allows for the analysis of heterogeneity in the effects of the program. Moreover, a deep knowledge of the objectives of the program as well as its administrative and institutional details can be important for the design of surveys that collect the right type of information to control for the selection process (Ravallion, 2008).<sup>37</sup>

> 37 Qualitative information, collected from surveys or focus groups, can complement quantitative survey data though it cannot be the basis for credible impact evaluation by itself.

28