rafmacalaba/datause-encoder-data huggingface dataset:
stage regressions for the harvests for children ages 2 to 5, and the point estimates are small and insignificant, suggesting a negative shock during these ages is less important than earlier years. Since the child‟s in utero, age 0, and age 1 periods are shown to be important (in the literature and in our first stage regressions), we estimate the first stage using those three instruments in Column 8. Point estimates are large and significant, with an F-statistic for the excluded instruments of 9.69, suggesting this strategy is valid. <mark>Rainfall for a child in utero that is more than one standard deviation below the village's long-run historical mean is correlated with 0.24 standard deviations lower ability. A rain shock for a child age 0 is correlated with 0.15 standard deviations lower ability, while a rain shock experienced by a child age 1 is correlated with 0.27 standard deviations lower ability.</mark> In Table 4, we present results from the household fixed effects instrumental variables regressions estimating the relationship between child cognitive ability and education outcomes and treating ability as endogenous. Results are consistent with the Table 2 OLS estimates, although the magnitude of the effects are larger, which we discuss in detail below. In treating child ability as endogenous, we use the three rain shock instruments for the time periods in utero, age zero, and age one.<sup>18</sup> A one standard deviation increase in child ability is correlated with an 81.7 percentage point higher likelihood of enrollment. To put this in perspective, a child that experiences a negative rain shock (rainfall one standard deviation below the village‟s historical long-run average) while in utero would have 0.235 standard deviations lower cognitive ability and this would lead to a 19.2 percentage point lower likelihood of enrollment, corresponding to a

> 18 Since the model is overidentified, we are able to test whether the instruments are uncorrelated with the error term and correctly excluded from the estimated enrollment equation. The overidentification test regresses the residuals from the IV regression on all of the instruments, and under the null hypothesis that all instruments are uncorrelated with the error term, a rejection of Hansen‟s J statistic casts doubt on the validity of the instruments. For the enrollment regression, the p-value of the J statistic is 0.3 indicating our instruments are valid, while for the other dependent variables in Tables 4 and 5, the p-values of the J statistic are generally slightly larger.

19
When the social gap between two individuals becomes too wide, the positive externalities for the poorer individual disappear.

My results show that social interactions matter. While this is not the first paper to find significant peer effects, this paper adds to a small set of studies that can identify causal peer effects that are not contaminated by endogenous sorting of pupils between schools. The size and significance of these estimates in a developing-country school system have important implications for social policy. Segregation exerts an effect on pupils through peer effects that cannot be overcome by equalizing school funding, pupilteacher ratios or syllabi. In that sense my results give concrete meaning to the U.S. Supreme Court’s dictum in 1954 that separate is inherently unequal.

The results also show that segregation is not a zero sum game, but may have aggregate consequences. The functional form used in previous analyses has largely ruled out the possibility of aggregate consequences from segregation by assumption. Relaxing these assumptions, I find somewhat troubling results, pointing to an equity-efficiency trade-off, with segregation yielding higher average scores and much higher inequality in scores between rich and poor. Nevertheless, the fact that inequality in achievement between rich and poor pupils appears in the simulation to be much more sensitive than mean scores to variation socioeconomic segregation may provide a cautionary note when formulating education policies.

# **References**

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- Ammermueller, A. & Pischke, J.-S. (2009). Peer effects in European primary schools: Evidence from the Progress in International Reading Literacy Study, _Journal of Labor Economics_ **27** (3): 315–347.

- Bedard, K. & Dhuey, E. (2006). The persistence of early childhood maturity: International evidence of long-run age effects, _Quarterly Journal of Economic_ **121** (4): 1437–1472.

- Brock, W. A. & Durlauf, S. N. (2001). Discrete choice with social interactions, _Review of Economic Studies_ **68** (2): 235260.

- Brock, W. A. & Durlauf, S. N. (2002). A multinomial-choice model of neighborhood effects, _American Economic Review_ **92** (2): 298–303.

29
As was the case for Eastern Europe, testing the log-linear specification against the linear form (Davidson and MacKinnon, 1981) demonstrated that the log-linear form was preferred. This means, for example, that the effect of adding an additional child is to decrease household welfare (expenditure per equivalent adult) in a fixed proportion, implying that the absolute costs of adding a child are lower for the poor.

In the FSU, locational factors have the strongest effect on household welfare, followed by the share of wages in household income, whether the household has a household enterprise, and higher education. These general findings are discussed in detail below.

In the FSU, the strongest effects on welfare were related to household location, with the sharpest change in household welfare (increasing it by 50 percent) implied by moving from a rural area to the capital in Kyrgyz Republic. Even moving from an urban area to the capital, Bishkek, would increase household welfare by one-third. The location effects are nearly as strong in Russia (43 percent rural-to-capital, 37 percent urban-tocapital) and not inconsiderable in Estonia (with rural-to-capital shifts increasing welfare by nearly one-third).

The dominant role of location, especially location in the capital city, has been documented in other FSU countries such as Armenia and Ukraine (World Bank 1996a, 1995c). In many ways, this finding demonstrates the slowness of transition and of business-encouraging reforms and private sector development, as well as questions of **scale** in many small FSU countries. Aside from Russia (and possibly Ukraine) most FSU countries are quite small in terms of population and GDP, so most private sector 72
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32
We stratified the randomization by whether we obtained the respondent through the branch vs. the mail, online or street survey, by gender, by having at least a bachelor’s degree or not, and by whether the person was (i) a client of our partner financial institution, (ii) a client of another financial institution, (iii) neither. Within the sample of financial institution clients, we further stratified by whether they made a deposit into their savings account during the past month and by whether they have a credit card. For clients with a credit card, we stratified by whether they made more than the minimum payment each month during the past six months. For individuals who were not financial institution clients, we stratified by whether they lived closer than 8 km away from a training location or not.

Our original intention with the mail screener survey was to study only individuals who are financial institution clients to learn whether the financial literacy course can improve their financial behavior and outcomes. Through the online, street, and branch surveys, we obtained 1,325 respondents who were not financial institution clients. We decided to keep these in the sample since the course material could in principle also be relevant for them and they may start financial institution relationships as a result of taking the course. However, the percentage of non-financial institution clients in the treatment group who ended up attending the financial literacy training was very low (18.1 percent), making it difficult to detect any effects on this sample. Since the take-up rates were higher among financial institution clients (28.1 percent), as discussed further below, we decided to conduct our follow-up survey only among financial institution clients and we drop non-financial institution clients from the impact analysis, although they are included in our experiments on inducing attendance.

Table 1 shows baseline variables collected through the screener survey for the sample of financial institution clients. About half of the individuals were clients of our partner financial institution as opposed to clients of another institution. Close to 65 percent made a savings deposit during the past month. About 40 percent had a credit card at baseline and only half of them made more than the minimum payment in all previous months. In fact, about 20 percent made a late payment on their credit card during the past six months. The demographic variables show that about half of the sample is female and 40 percent has at least a bachelor’s degree. The average age is 33 years. As expected given the random assignment, all baseline variables are balanced across the treatment and control groups.

# **4.5 Initial Take-Up: Low Attendance for Training Even among Those Who Say They Are Interested in Attending a Financial Literacy Course**

Starting on August 1, 2011, each person in the treatment group was contacted by telephone and invited to participate in the financial literacy training program. If the participant confirmed 14
status.<sup>11</sup> Given that firms are not randomly privatized and that workers could also sort into state-owned companies, selection bias is a particular concern in our empirical strategy. To mitigate these concerns, we build a control group of similar workers and SOEs that are not part of a privatization event.<sup>12</sup> The framework compares the evolution of wages for workers in privatized firms to the one of similar workers in non-privatized companies. In doing so, we use a sample of workers from 2011 to 2020 and apply an event-study method. To avoid capturing false privatizations, we exclude cases in which firms switch between public and private status more than once during the whole period.

Methodologically, we follow a growing literature on the effects of privatization and combine matching techniques with difference-in-differences (DiD) methods (see Arnold, 2022; Olsson and T ̊ag, 2021; Bastos et al., 2014). In the first stage, we take the sample of privatized and non-privatized SOEs and build a control group based on workers’ characteristics. In particular, for each year, we limit our sample to sectors with at least one privatized and non-privatized company and apply the CEM matching algorithm (Iacus et al., 2012) on workers’ wage, age, gender, occupation, tenure, education, and firm size. In the second stage, we stack cohorts of matched individuals in the treatment and control groups and estimate the following specification: where _yit_ is the outcome of interest, the relative monthly salary, or the probability of layoff.<sup>13</sup> Relative wages are measured compared to worker’s compensation in _t −_ 1, while layoff is a dummy equal to one if the worker is unemployed in a given period. Wages are taken as zero whenever the individuals are unemployed. _Ti_ is a treatment indicator that is equal to one if the worker was employed in a firm that privatized and zeroes otherwise, and _νt_ represents time-to-event dummies from two years before the event to three years after privatization (t-1 is the baseline). _λi_ and _θt_ account for individual and year fixed effects, and _δs_ and _σj_ are sector and region dummies.

Figure 2 shows the effects of privatization on workers’ relative wages. In panel (a), we observe that the coefficients are non-different from zero until _t_ , thus indicating that workers from the treatment and control groups had similar trajectories until the year of privatization. Following the privatization of SOEs, individuals in privatized firms faced a substantial wage

> 11Tables A3, A4, A5 and A6 in the Appendix present the transition matrices describing changes in firm ownership to illustrate the number of privatization cases in our sample, both in terms of percentages and event frequencies.

> 12Appendix D shows that privatized SOEs do not pay a larger wage premium than non-privatized SOEs. 13 We use monthly wages to have comparable results with Arnold (2022).

28
**Figure 2: Poverty impacts of disbursements under Argentina’s Trabajar program**

<!-- Start of picture text --> 1<br>.8<br> (1)<br>.6<br> (2)<br>.4<br>.2<br>0<br>0 100 200 300 400 500 600 700<br>Incom per capitae<br><!-- End of picture text -->

- (1) Participant sample pre-intervention (estimated)

- (2) Participant sample post-intervention (observed)

Source: Jalan and Ravallion (2003b).

62
of household could thus introduce a downward bias to our labor supply estimates. The final sample is a balanced panel of 2,329 individuals of whom 1,734 (74.4 percent) are women. The sample is heavily skewed towards women because households are overwhelmingly headed by males.

In Table 5 (6), we provide sample means from ALSMS02 and the results from the weighted tests of mean differences by household NE (old-age pension) recipient status. The tests of mean differences in individual characteristics were run among _work eligible individuals_ , whereas the tests of mean differences in household-level variables were computed among _households_ . 2005, as opposed to 2002, descriptive comparisons do not yield different results with respect to the findings reported here. The majority of the mean differences reported in Table 5 are statistically significant at the 1% level. We observe that work eligible individuals from NE households, on average, work less (in terms of hours or weeks of labor supplied), and are less likely to have worked in the past 7 days in comparison to their counterparts from non-NE households. In contrast, Table 6 shows that work eligible individuals from pension households are more likely to have worked the last seven days and work longer hours and more weeks with respect to comparable members of non-pension households, these differences are however small in magnitude. Although work-eligible individuals from NE households are less educated than their comparators from non-NE households, the comparison of years of education by household old-age pension recipient status yields the opposite result.

Furthermore, while NE households record, on average, lower per capita consumption than non-NE households, the test of mean differences in the same variable by household old-age pension recipient status does not lead to a statistically significant finding. Despite the fact that the average amount of land owned by NE households is significantly lower, these units record 15
biguous and potentially non-linear, with large firms more able to privatize their own security provision (and thus become resilient to insecurity) and better equipped to adjust their areas of operation, but also more exposed to risks associated with their level of investment and public profile.

Three key questions arise at this time, which we are pursuing in ongoing work. First, when do the effects we observe constitute a temporary displacement of firm activity versus a permanent change in where some firms will operate? Second, what additional insight can be gained on the mechanisms behind the firm-level responses we find here? Rising insecurity may signal substantive increases in the fixed and variable costs of operating a business, including disruptions to the labor supply, threats to capital investments, new operating costs from private security provision and various forms of predation, as well as decreases in demand from local and international buyers. To develop more effective business and policy responses, it is crucial to better understand the relative importance of such channels, as well as the understudied role of perceptions of insecurity as distinct from observed realities. Third, how are firms adapting to persistent insecurity, which at this stage has lasted years if not decades. For example, are they more likely to privatize their security provision (which may only make sense given a certain scale of operations), or to restrict growth and attempt to “fly under the radar” to mitigate risk to property and self, and which approaches are associated with greater firm survival?

# **5 Conclusion**

To our knowledge, ours is the first study to use call detail records of mobile phone subscribers to understand firm behavior in a conflict-affected country, or indeed in any developing country. From a methodological standpoint, the validation exercises in this study suggest the promise of this approach - not as a substitute to the crucial work of collecting survey and administrative data on firms in such settings, but as a complement, particularly in fragile 24
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76
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|Strongly|(0.248)|(1.267)|(9.431)|
|---|---|---|---|
|agrees or||||
|agrees that it<br>is acceptable<br>for "a man to<br>beat his||||
|partner in the<br>case of||||
|infidelity"||||
|Antofagasta|0.623*|0.871|0.486|
|Region|(0.157)|(0.658)|(0.281)|
|Atacama|0.724|0.179|0.403|
|Region|(0.184)|(0.206)|(0.257)|
|Coquimbo<br>|0.943|2.101|1.253|
|Region|(0.244)|(1.385)|(0.657)|
|Valparaiso|<br>0.578**|<br>0.913|<br>0.674|
|Region|(0.154)|(0.631)|(0.384)|
|O ́Higgins<br>|1.122|0.935|1.908|
|Region|(0.292)|(0.749)|(1.025)|
|Maule Region|<br>1.069|<br>0.109*|<br>1.849|
||(0.291)|(0.127)|(0.926)|
|Biobio Region|0.838|0.275|1.321|
||(0.224)|(0.327)|(0.726)|
|Araucania<br>|0.716|0.701|0.356|
|Region|(0.193)|(0.556)|(0.226)|
|Los Lagos|0.356***|0.155*|0.348|
|Region|(0.118)|(0.148)|(0.239)|
|Aysen Region|1.273|0.773|0.815|
||(0.345)|(0.606)|(0.519)|
|Magallanes|0.569*|0.561|0.159*|
|Region|(0.167)|(0.471)|(0.155)|
|Metropolitan<br>|0.741|0.527|0.722|
|Region|(0.160)|(0.354)|(0.341)|
|Los Ríos|<br>1.064|<br>0.441|<br>1.344|
|Region|(0.259)|(0.405)|(0.757)|
|Arica and|1.081|0.802|0.733|
|Parinacota||||
|Region|(0.283)|(0.611)|(0.450)|
|Ñuble Region|0.928|1.247|1.469|
||(0.243)|(0.921)|(0.898)|
|Constant|0.483*|0.0415***|0.154**|
||(0.202)|(0.0450)|(0.114)|
|Observations|3,615|3,615|3,615|
|LR chi2()|786.9|786.9|786.9|

17