rafmacalaba/datause-encoder-data huggingface dataset:
Finally, to verify that the results are driven by managers trading relative to their peers and not by trading relative to a broad market benchmark, I calculate _Market Distance_ as the difference between the IGBC index weight on stock _s_ and fund _i_ ’s weight in stock _s_ for each period, _Market_<sup>_i_</sup> _st_<sup>= Π</sup><sup>_IGBC_</sup> _st − wst_<sup>_i_.</sup> The IGBC is a widely used value and liquidity based index for the Colombian stock market. I also interact this measure with relative performance.

This previous specification is motivated by Basak et al. (2007), who find different behavior in U.S. equity mutual funds depending on whether managers are ahead or behind the S&P 500 index. In their specification, the authors define _risk shifting_ as an increase in the absolute difference between a fund’s returns and the S&P 500 returns. They regress this variable on an interaction between current relative returns and the market returns. Their question is whether underperforming funds move towards or away from the market index, thereby increasing or decreasing the size of deviations from market returns. My specification is analogous to theirs, in that one of my objectives is to measure whether underperforming funds move towards or away from a reference portfolio, the peers’ portfolio ( **F3** ), by increasing or decreasing their holdings of stocks in which they are underexposed or overexposed. Note that while Basak et al. (2007) only observe return outcomes, I observe portfolio weights and thus the actual strategy of the manager. In a setting with a small number of managers it might be hard to distinguish if changes in the cross-section dispersion of returns are due to managers’ strategies or to the realization of stock returns.

# [Insert Table 3 about here]

Table 3 documents the results of the linear regression for adjusted weight changes ∆ _wst_<sup>_i_.Theresults</sup> suggest that regardless of relative performance, managers were more likely to increase their holdings of stocks in which they were already overexposed after the MRG was loosened in June 2007 than before this date. That is, there was less trading towards peers once the MRG was loosened. This change in behavior associated with the change in regulation is consistent with the average behavior of trading direction presented in Figure 2 and Table 2.

Figure 3 presents differences in marginal effects of _distance_ on adjustments in portfolio weights before _∂_ ∆ _w_ <u>(</u> _MRG_ =1) _−_<sup>_∂_∆</sup><sup>_w_</sup><sup><u>(</u></sup><sup>_MRG_=0)</sup> and after the policy change _∂d ∂d_ along with corresponding confidence intervals. � � Underperforming managers ( _rel <_ 0) were more likely to increase their holdings of stocks in which they were underexposed ( _d >_ 0) prior to June 2007 than after this date. This result for individual stocks is consistent with the decrease after June 2007 in the correlation between direction and relative performance documented in Table 2-Panel C. To give a sense of the quantitative importance of these estimates, the 11
Table 2: Summary of Pre-MNREGA Economic, Agricultural and Fire data

|Phase 1<br>(1)|Phase 2<br>(2)|Phase 3<br>(3)|
|---|---|---|
|**Data from 2001 Census**<br>|||
|Total Population (000s)<br>1,712.12|1,772.15|1,693.61|
|Total Households (000s)<br>320.12|326.19|320.43|
|% Rural<br>0.84|0.83|0.73|
|% Urban<br>0.16|0.17|0.27|
|% Scheduled Castes<br>0.15|0.15|0.15|
|% Literate<br>0.48|0.52|0.57|
|% with domestic electricity<br>0.88|0.87|0.91|
|% with agricultural electricity<br>0.74|0.59|0.72|
|% with electricty<br>0.75|0.65|0.74|
|% Paved road<br>0.49|0.56|0.68|
|% Mud road<br>0.82|0.82|0.76|
|**Data from 2011 Census, 2012 SECC and VC**|**F Data**||
|Distance to nearest place with _>_100k population<br>50.78|41.87|40.74|
|Per capita consumption, rural<br>15.64|16.59|19.02|
|% HH with cultivation as main income<br>0.35|0.37|0.38|
|Avg. Forest Cover, 2002-05<br>11.31|15.15|13.34|
|Avg. Night Lights<br>29.50|27.93|61.63|
|**Data from NASA FIRMS**|||
|Monthly Fires prior to MNREGA<br>3.61|3.73|7.33|
|**Data from ICRISAT, Planning Commission and 200**|**6 Input **|**Survey**|
|Avg. Per Capita GDP, Ag<br>3.70|4.22|4.90|
|Avg. Per Capita GDP<br>14.39|15.13|21.26|
|Avg. Area Planted in Sugarcane (000s HA)<br>5.86|5.71|10.36|
|Avg. Area Planted in Rice (000s HA)<br>102.43|117.19|58.77|
|Avg. Area Planted in Wheat (000s HA)<br>39.76|57.85|61.63|
|Avg. Area Planted in Other Crops (000s HA)<br>172.67|165.39|207.96|
|Share of holdings _>_4 HA<br>0.26|0.28|0.33|
|Combines in 2006 (000s)<br>1.41|1.12|1.41|

Notes: Columns 1-3 report the mean of the named variable by district according to the MNREGA phase of that district. Data from the 2001 Census, the 2011 Census, the 2012 SECC and the VCF data come from the SHRUG dataset (Asher et al., 2019). Fire data is downloaded and assembled from the NASA FIRMS data and is derived from imagery from the MODIS satellite. ICRISAT data comes from the ICRISAT meso dataset (Rao et al., 2012). GDP data is scraped from the Indian Planning Commission website and covers the years 2003-2005 for most districts. Information on combines is scraped from the Indian Ministry of Agriculture website and comes from the 2006 Agricultural Input survey.

38
**Figure 4. 27. Central water and electricity 24 hours a day**

(for apartment dwellers only) <!-- Start of picture text --> Capital Other Urban Rural<br>100<br>80<br>60<br>%<br>40<br>20<br>0<br>Albania Bosnia* Georgia Armenia * Kazakhstan Kyrgyz Tajikistan Turkmenistan<br>Balkans/EE Caucasus Central Asia<br>Water Electricity Water Electricity Water Electricity Water Electricity Water Electricity Water Electricity Water Electricity Water Electricity<br><!-- End of picture text -->

* Bosnia urban, mixed, rural settlement.  * Armenia -electricity reliability not available.  * Kyrgyz water reliability not available

Source: see Table 2.1 As might be expected, apartment dwellers are generally more likely to be connected to network utility services than the rest of the population. But at the same time, service provision is not reliable and apartment dwellers have limited coping options, such as carrying water or using alternative power sources.<sup>36</sup> Despite being relatively well-off, many of the apartment dwellers are infrastructure-poor in terms of the adequacy of service given their limited alternatives. In most of the countries sampled, water and/or electricity service is available 24 hours a day to fewer than half of apartment residents. In Albania, fewer than 40 percent of apartment dwellers in the capital receive water 24 hours a day, while in other cities, the share drops to 25 percent. In Armenia, where 68 percent of capital city residents and 57 percent of those in other cities live in apartments, fewer than 15 percent receive uninterrupted water supply. In secondary cities in Georgia, water and electricity are regularly available to fewer than 20 percent of apartment residents and the collapse in services to apartments has made life very difficult as the Box 4.3 shows.

# **Box 4.3.  Living without services in Georgian apartment buildings**

Most municipal heating systems have stopped supplying households with hot water, heating, and also cooking gas. As a result, when electricity is available, households use electric heaters or hot plates to heat and cook. Lack of electricity makes it difficult to warm homes, prepare hot meals, watch television, or listen to radio; often telephones ceased to function as well. High-rise elevators stop running. Pumps stop supplying water to upper stories of high rise apartment buildings, forcing occupants to carry water up many flights of stairs every day. In winter, most people conserve heating fuel by moving into one room, and using alternative fuels and strategies to survive.

Source: Background paper on Georgia for “When Things Fall Apart.” 36 The survey data used for this study indicate that apartment dwellers who are connected to district heating generally do have 24 hour service. District heating in Turkmenistan, and natural gas in Georgia and Kazakhstan, were significantly more interrupted for apartment residents in other urban areas. (Data were very limited on natural gas.) 44
# **Leaning in at Home: Women’s Promotions and Intra-household Bargaining in Bangladesh**

Hannah Uckat, World Bank<sup>*</sup> _JEL codes:_ D13, J16, J21, M51, O14 _Keywords:_ Gender and Economic Empowerment, Decision Making and Poverty, Career Management, Jobs, Textiles and Wear

> *The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent. I thank Christopher Woodruff and Simon Quinn for invaluable advice and support. The paper has benefited greatly from discussions with and comments by Abi Adams, David Atkin, Abigail Barr, Girija Borker, Laura Boudreau, Emily Breza, Leonardo Bursztyn, Elwyn Davies, Cheryl Doss, James Fenske, Douglas Gollin, Rachel Heath, Dahyeon Jeong, Erin Kelley, Matthew Klein, Florence Kondylis, Arianna Legovini, Benedetta Lerva, Paula López-Peña, David McKenzie, Amanda Pallais, Natalie Quinn, Natalia Rigol, Heather Schofield, Tavneet Suri, Kate Vyborny, and from audiences at the German Development Economics Conference 2022, CSAE Conference 2022, World Bank 2020, NEUDC 2019, Advances for Field Experiments 2019, Empirical Management Conference 2019, OxDev 2019, CSAE Workshop 2019, EDI Workshop 2017, and OxFLO 2017-18. The project would not have been possible without the cooperation of participating factories and workers, and the excellent Innovations for Poverty Action (IPA) field team. I gratefully acknowledge funding for the surveys for this project by the Private Enterprise Development in Low-Income Countries research initiative (PEDL); and the Economic Development and Institutions research program (EDI), funded by UK aid from the UK government. The promotion program was funded by the International Finance Corporation and the Urban Services Initiative, and run in co-operation with BetterWork Bangladesh, a program of the International labor Organization. This study, together with Uckat and Woodruff (2020), was registered with the AER RCT Registry as AEARCTR-0001843, and received ethical approval from the University of Oxford and Innovations for Poverty Action. The reproducibility of the exhibits in this paper has been confirmed by DIME Analytics pre-publication code review.
(enrolling in a bachelor’s program, enrolling in a SC program, or not enrolling in higher education), which might bias OLS estimates of labor market impacts. Second, while a standard Instrumental Variables (IV) approach could address self-selection issues in homogeneous treatment effect settings, under general conditions it would not identify the average effect of SC programs (Heckman and Urzúa, 2010). More precisely, in our essential heterogeneity setting, a standard IV strategy would only identify the effect of SC programs on compliers relative to the next-best option that the student would have otherwise chosen–enrolling in a bachelor’s program or not enrolling at all in higher education–without identifying the separate margins of choice. In other words, a standard IV strategy would identify the effect of SC programs relative to a mixture of the other two options. Only under additional assumptions could one decompose this effect into its sub-components and provide the underlying pairwise comparisons (as in Kline and Walters, 2016; Hull, 2018). Rather than impose additional assumptions, we exploit rich student longitudinal data and local exogenous variation in higher education supply to estimate the share of students who respond along each margin of choice–expansion and diversion–while also estimating SC programs’ labor market effects relative to the next-best option.

Evidence on these margins is novel for developing countries. While other studies have explored higher education returns in developing countries, they have either compared returns across countries (Ferreyra et al., 2017, 2021) or, within a country, have estimated returns for new _versus_ existing programs (Camacho et al., 2017), by program and field (Ferreyra et al., 2020), or for selective institutions (Barrera-Osorio and Bayona-Rodríguez, 2019). Unlike previous studies, we quantify the margins of choice and argue that these are critical to who benefits from SC programs, and why. Consider, for instance, a policymaker who builds a new higher education institution (HEI) specialized in SC programs. This might lead some students (the compliers) to enroll in SC programs even though they would not have done it otherwise, perhaps leading the policymaker to believe that all compliers would benefit from the new SC programs and improve their labor market outcomes. Whether this happens, however, depends on students’ next-best option. For a student who would not have attended higher education, the SC program might indeed raise human capital and improve labor market outcomes. For a student who would have attended a relatively good bachelor’s program and for whom the SC program might be an “undermatch”, labor market outcomes might become worse. Yet, for a student who would have otherwise attended a low-quality bachelor’s program and for whom the SC program might provide a better match, labor market outcomes might actually improve. Because individuals differ in their next-best option based on their personal background and local opportunities, the policymaker should not necessarily expect average positive 3
# **_4.4 Conversion Factor: Converting the Number of Accounts to the Number of Account Holding Individuals_**

It is possible to convert our data and estimates of the number of accounts in each country into rough estimates of the number of banked individuals in each country. To do so, we have to estimate a conversion factor, which is the number of accounts in a country, per banked individual in each country.<sup>19</sup> We use data from household surveys to estimate the number of individuals who have savings accounts in formal financial institutions (which could be any of our institutional categories) and divide the number of accounts in the country by this number.

We begin by evaluating whether our main measure of deposit account penetration, namely the number of accounts per thousand adults, are significantly correlated with some more accurate indicators of financial access, which are available for some countries through household surveys. A regression of the reported rates of formal account ownership from household surveys on our proxy for deposit penetration, namely number of accounts per thousand adults (in logarithms), shows that the deposit penetration indicator is a good predictor of true financial inclusion, at least in the limited sample of countries for which we have comparable household level data. Figure 1 shows the added variable plot for the log of deposit penetration; the fit is very close. Next, Table 14 shows the results of three bivariate regressions with rates of account ownership from household surveys on the LHS and log of deposit penetration on the RHS. In the first model, only surveys completed since 2003 are included, in the second model, the sample is further restricted to surveys which have all adults as the survey frame (as opposed to all households), the final column are all available surveys (which go back to 2000). The coefficients are largely similar across the three samples, and the R<sup>2</sup> is 0.69 and 0.71 when only more recent (and thus more accurate) surveys are used. These results confirm that the deposit penetration ratio can be used to predict the percent of the population with a bank account to a fair degree of accuracy. Table 17 provides a list of household survey data and the sources.

> 19 This is not necessarily the same as the average number of accounts held by each account holder since business and government accounts will be counted in the numerator.

22
distance in time across different treatment periods across countries. The latter term is a new addition compared to estimators used previously in the literature. The two parameters allow weighting the difference between treated and control units (from the TWFE component) by how much the two are comparable.<sup>14</sup> We use the SDID estimator to identify the Average Treatment effect on the Treated (hereafter, the ATT) of signing a PTA containing at least one NTP addressing one of the three policy domains of interest: environmental protection, labor market regulation, and civil and human rights promotion. We consider a country as “treated” if it signs an agreement that includes the provision of interest in a given year.<sup>15</sup> Following the synthetic control and DID literature, we include a set of additional country characteristics to improve the matching between PTA signatories and control units. Annex Table A-3 A reports the basic summary statistics for the covariates included in the matching algorithm of the SDID. We include three measures of market size and wealth (GDP, population and GDP per capita), a measure of government accountability as a proxy for the likelihood a government will comply with international agreements (from the WDI database), the value of total exports and the share of total exports accounted for by the EU and the US, respectively. All else equal, greater trade dependence is likely to increase implementation of NTPs. Similarly, greater reliance on trade with the EU and the US (the two major proponents of NTPs globally) is also more likely to improve compliance.

# _3.2 Results: Non-binding provisions_

We first investigate the impact of non-binding NTPs on related non-trade outcome indicators. We compare outcomes in countries signing non-binding NTPs to those observed in countries that do not sign any agreements including the relevant NTPs (i.e., we exclude those countries that, at some point before or during the sample period sign a PTA with

> 14Most of the tests showing the consistency of SDID under different weighting schemes performed by Arkhangelsky _et al._ (2021) are based on a single treated unit. We exploit the foundation for the staggered treatment scenario in their Appendix A, where they allow for multiple treated units and multiple treatment periods. Pailañir and Clarke (2022) implement both procedures in STATA, allowing for the inclusion of additional covariates to improve the matching in the pre-treatment period.

> 15If a country has signed more than one agreement containing the same provision in the period of interest, the earlier one is chosen.

13
children pass at least one stage and 0 otherwise. Thus ECED enrollment and the test of executive function are measured in percentage points while all other outcomes are measured in standard deviation units. The visible patterns are as follows.

First, at baseline most of the outcomes for children in batch 1 villages are better than those for children in batch 3 villages and for children in villages without the project. This is to be expected because batch 1 villages had been receiving the ECED project services for about 6 months at baseline. Baseline ECED enrollment for batch 1 children is 61% - much higher than for batch 3 children (34%) and children in villages without the project (36%).

Second, at baseline most outcomes for children in batch 3 villages are similar to those for children in villages without the project. As we discussed earlier, a group of villages was identified by government officials to make a comparison group for batches 1 and 3. Because of the early implementation of the program in batch 1, we cannot compare batch 1 villages with this comparison group of villages. However, we can check whether batch 3 villages are comparable to these villages without the project in terms of enrollment and child outcomes. We find that they are very similar to each other at baseline. None of the outcomes are statistically different between two groups. The ECED enrollment at baseline is 34% and 36% for batch 3 villages and those without the project, respectively and other child outcomes are also very similar. The close comparability of these two groups of villages is highly encouraging for us to use a difference-indifferences (DiD) approach to examine the impact of the ECED project on enrollment and child outcomes.

Third, for children in all batches most outcomes show improvements during the time that elapsed between baseline and follow-up. In other words, children grew up and measures of their development improved even in the absence of the project. ECED enrollment also increases over time, even for villages that did not receive the ECED project. This reminds us that we need to control for improvements in outcomes driven only by aging. Therefore, we have a time dummy in the DiD model to control for the effect of age. Our DiD estimators yield the exclusive impact of the ECED project after accounting for the effect of age on child development.

In Table 3, we compare key characteristics of children who were not enrolled in ECED services at baseline depending on whether they live in project villages or non-project villages and examine their families’ enrollment decisions at the time of the follow-up. We note that at baseline, children who did not enroll in ECED services have very similar levels of low parental 11
Table D15: Ethnicity randomization checks, 2011 and after, 4

||(1)|(2)|(3)|
|---|---|---|---|
||Judge plur. Pokot|Judge plur. Somali|Judge plur. Turkana|
|Pla. plur. Pokot|-0.00227<br>(0.00281)|||
|Def. plur. Pokot|-0.000560<br>(0.00171)|||
|Pla. plur. Somali||0.00220<br>(0.00364)||
|Def. plur. Somali||-0.00161<br>(0.00244)||
|Pla. plur. Turkana|||0.000157<br>(0.000191)|
|Def. plur. Turkana|||-0.00111<br>(0.00120)|
|DV mean|0.00321|0.00760|0.000591|
|Court-year FE|Yes|Yes|Yes|
|Ethnicity dummies||||
|Other controls|Yes|Yes|Yes|
|Observations|11838|11838|11838|

The regressions test whether female plaintiffs/defendants are more likely to be matched with judges of their own ethnicity than judges of other ethnicities.Standard errors, in parentheses, are clustered at the judge level. All columns are based on a linear regression model. For specification details, see equation 2. Sample is restricted to the years 2011-2020. Other controls include case type dummies, a dummy for an appeal case, and variables for the numbers of defendants, plaintiffs, and judges. To prevent a loss of observations, all categorical controls (such as case type) include a dummy that denotes if data is missing/unknown. Pla. = plaintiffs, def. = defendants, plur. = plurality, maj. = majority.

51
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