rafmacalaba/data-use-mentions-extended huggingface dataset:
state that they need electricity to run their businesses. In contrast, the HE-SE have little need for water while employers particularly need this service.

Electricity needs are generally met across firm types while water needs are not. Again turning to the IES survey, among those informal firms needing electricity, 76.9 percent are connected to the grid, with HE-SE having greater connectivity than the others (Figure 21). The conditional estimates confirm that those who are connected to the grid are more likely to be employers and less likely to be LE-SE. Water access is a different story. Among those needing water, only 24.5 percent have full access, again, with HE-SE having more access than the others. The conditional estimates find that LE-SE have particular water deficiencies (Table 4). This in contrast to water and electricity access in the homes of workers. If we consider all workers (rather than firms) surveyed in the GMD, regardless of whether they need water or electricity, we find high access to water and electricity in their homes, about 80 percent access for each (Figure 22), with few differences between formal and informal workers. Access to improved sanitation is markedly lower for informal workers than formal sector workers.

Informal workers and firms’ absolute and relative access to the internet is low, with significant variation across employment types. Only 40.6 percent of informal workers have access to the internet, with particularly low connectivity among the unpaid and LE-SE (Figure 22). The conditional correlates, controlling for poverty level, confirm that those workers with access to the internet are less likely to be unpaid or LE-SE as compared to all other job types (Table 5). The HE-SE have internet access on par with formal wage employees (58 percent) (Figure 22).

Cell phone access is much higher than internet access and relatively equal across employment types. It exceeds 80 percent for all employment types except LE-SE (76.4 percent), with the HE-SE having the most access (
# **2. Literature Review and Theoretical Expectations**

# **2.1 Recent literature**

The literature on the gender-level impacts of armed conflicts has been growing in recent years due to improved access to household level data for conflict-affected economies. This section briefly reviews studies that address the effect of armed conflict and large-scale economy-wide disruptions on the education and labor market outcomes of individuals that were either exposed to the conflict as civilians or through participation in the military.

The research on the relationship between armed conflict and education began with an examination of cross-country differences in aggregate enrollment rates in developing and developed countries (Stewart, Huang and Wang 2001). Once individual and household level datasets became available, researchers turned to the examination of the impact of conflict on differences in educational attainment across birth cohorts and regions (Merrouche 2006; Akresh and de Walque 2008; Shemyakina, 2011). These studies observe a decline in the education of affected cohorts but do not reach the same conclusions. Akresh and de Walque find that the education of boys from wealthy households suffers due to the genocide in Rwanda, while Shemyakina’s analysis indicates that in Tajikistan the impact is stronger for older girls from affected household as compared to younger girls from similar households. These studies contemplate that the observed decline in education may be related to school closure, migration and displacement, quality and availability of school facilities and shocks to income and security. The studies also note that the observed decline in education is likely to have a negative impact on the future productivity and wages of affected cohorts.

Two recent studies connect large economic and political shocks to labor market experience and education. Meng and Gregory (2007) investigate the impact of the Chinese Cultural Revolution on the earnings of the cohort who lost a substantial number of years of education due to the Revolution. They find that the earnings of the individuals who did not receive university degrees (but would have if they had been raised during a different period) were about 46-76 percent lower. Blattman and Annan
Senik, 2010).

Table 2 presents a test of this mechanism using LiTS data. LiTS surveys, being only representative at the country level, don’t provide sufficient sample size for an accurate estimation of respondents’ position in the income distribution of their locality, which is the reference group used in Cruces et al.’s analysis. Given the information available in LiTS we propose two alternative reference groups: (1) individuals with the same educational level (defined as either university education or less than university education) living in the same region within a country; (2) individuals with the same age (for which there are three age groups - below 35 years, between 35 and 55, and over 55 years of age) and same educational level within a country. Whenever the respondent’s region is not available, the country as a whole is used. A simple linear regression of the perceived decile as dependent variable, and the objective decile and the rank within the reference group as independent variables is estimated by OLS. The results of table 2 show that, conditional on the inclusion of the objective consumption decile and a series of individual level controls, the respondent’s rank within either type of reference group is not correlated positively with the perceived position in the income distribution - if anything, in 12
008)|(0.013)|
|Riskft* MPft||||-0.003|-0.018***|-0.018*|
|||||(0.004)|(0.005)|(0.010)|
|Earmarkfbt* MPft||||0.002*|0.004|-0.032**|
|||||(0.001)|(0.006)|(0.013)|
|Observations|259,709|179,786|182,955|259,709|179,786|182,955|
|R-squared|0.868|0.910|0.916|0.868|0.910|0.916|
|Mean loan volume (logs)|11.05|11|11.08|11.05|11|11.08|
|Firm*Bank FE|Yes|Yes|Yes|Yes|Yes|Yes|
|Bank*Month FE|Yes|Yes|Yes|Yes|Yes|Yes|
|Location*Sector*Month FE|No|Yes|No|No|Yes|No|
|Firm*Year FE|No|No|Yes|No|No|Yes|
|Notes: The table shows estimates of OLS regres<br>relationship with a bank. The dependent variable<br>consecutive periods after a firm receives its first<br>prior to the start of their earmarked relationship<br>prior to the start of their earmarked credit relation<br>(measured by the Herfindahl Index) is above the<br>loan characteristics at the time of issuance (matu<br>effects for the ten loan rating categories establis<br>Brazil's CDI). Standard errors are doubled cluster|sions on our loan-level data<br>corresponds to the volume of<br>
Supplementary Table 5. Directory of variables in the individual-level dataset

|**Variable name**|**Label**|**Data processing notes**|**Additional notes**|
|---|---|---|---|
|_indiv_id_obs_|Individual ID<br>(panel<br>identificator)|Variable created by assigning<br>a numeric code to each unique<br>individual. The first number<br>of the code determines the<br>country.||
|_indiv_id_merge_|Individual ID<br>(to merge<br>with raw data)|<br>ID to merge with raw LSMS<br>data|Can be merged with the following<br>variables in the raw data<br>(concatenated variables are separated<br>by hyphens):<br>ETH:_individual_id_(wave 1)_,_<br>_individual_id2_(wave 2)_,_<br>_individual_id2_(wave 3)_,_<br>concatenation of_household_id_and<br>_individual_id_, (wave 4)_,_<br>concatenation of_household_id_and<br>_individual_id_(wave 5)<br>MWI:_PID_(wave 1),_PID_(wave 2)_,_<br>_PID_(wave 3)_, PID_(wave 4)<br>MLI: concatenation of_grappe_<br>_menage,_and_numero d’ordre_(wave<br>1), concatenation of_grappe_<br>_exploitation_and_numero d’ordre_<br>(wave 2)<br>NER: concatenation of_hhid_and<br>_numero d’ordre_(wave 1)_,_<br>concatenation of_GRAPPE,_<br>_MENAGE, EXTENSION_and_numero_<br>_d’ordre_(wave 2)<br>NGA: concatenation of_hhid_and_id_<br>(wave 1)_,_concatenation of_hhid_and<br>_id_(wave 2)_,_concatenation of_hhid_
0.00|0.00|0.00|0.00|0.00|
|Shrimp|-0.05|0.05|0.00|-0.05|-0.01|-0.04|-0.03|
|Soya|0.00|0.00|0.00|0.00|0.00|0.00|0.00|
|Sugar|0.09|0.11|0.19|-0.10|-0.04|0.04|0.08|
|Tea|0.13|0.06|0.18|-0.04|0.07|0.15|0.08|
|Tomato|0.03|0.02|0.04|-0.00|0.01|0.03|0.02|
|Vanilla|0.00|0.00|0.00|0.00|0.00|0.00|0.00|
|Vegetable oils|0.00|0.00|0.00|0.00|0.00|0.00|0.00|
|Wheat|0.01|0.00|0.01|0.00|0.00|0.01|0.01|
|Wine|0.00|0.00|0.00|0.00|0.00|0.00|0.00|

Notes: Authors’ calculations based on HIT data. The table presents the gains associated with the (country by country) elimination of Vietnam’s own agricultural import tariffs.

35
crop cutting experiments. For example, the insurer could conduct or co-observe a sample of crop cutting experiments across the state and use this data to estimate the manipulation-free aggregate claim payment to be paid to farmers in the state. If the aggregate state-wide claim payment rate arising from the full set of crop cutting experiments is sufficiently higher than this manipulation-free estimate based on the manipulation-free sample, then the insurer has reasonable grounds for believing that there has been systematic manipulation of crop cutting experiments across the state. Conducting random audits of, say, 5% of all CCEs would be much less expensive than conducting audits of all CCEs. However, for random auditing to be effective, the maximum punishment in the event of detected manipulation of CCEs must be large enough to deter manipulation. The threat of future exclusion from the mNAIS may be sufficient to ensure that states conduct sufficient monitoring of their employees. Insurers could also incorporate independent data, such as remote sensing or weather station data, in their validation of CCEs.

**Learning how to increase outreach** : Currently, most of the insured farming households are covered on a compulsory basis, with 95 million farming households not insured. With a subsidized premium, improved product design and faster claim settlement, the mNAIS product should be attractive to most farmer households across India: most farmers will pay around a third of the commercial premium and for every 1 rupee paid in premium will expect to receive approximately 2 rupees in claim payments.  (Whilst this was true on an aggregate basis under the NAIS, expected claim payments were not evenly distributed between insurance units and so NAIS was poor value for some farmers.). However, designing a good insurance product is not enough to guarantee voluntary purchase; insurance is never bought, always sold. If the mNAIS is to offer protection to the poorest, most vulnerable farmers, insurers must actively market the product to these farmers.

Communication is particularly important since farmers who, under NAIS, were paying a maximum premium rate of 3.5% may
031|(0.029)||-0.030|(0.029)||
|_VUL_|-0.025|(0.008)|***|-0.024|(0.008)|***|
|_RD_|1.911|0.5694|***|1.848|0.5678|***|
|_ALLWEARD_|0.149|(0.071)|**|0.152|(0.071)|**|
|_RICE_|-0.019|(0.163)||-0.080|(0.164)||
|_AMENITY_|1.552|(0.782)|**|1.558|(0.771)|**|
|_TAXIBE_|0.142|(0.087)|*|0.157|(0.087)|*|
|_SUBU_|-0.027|(0.059)||-0.037|(0.059)||
|Constant|6.938|(3.825)|*|5.152|(3.222)||
|Obs.|548|||548|||
|No. of district|||||||
|dummies|3|||3|||
|Wald chi2|139.05|||142.39|||
|Spatial parameters:|||||||
|_λ_|0.187|(0.356)||0.290|(0.329)||
|_ρ_|3.549|(0.708)|***|3.453|(0.746)|***|
|Hausman endogeneity<br>Chi2 test statistic|test:<br>8.680||
|2793|2793|2793|

_Notes_ : To remove the influence of outliers in the dependent variable, we drop households in the top 1 percent of the distribution of total borrowing. SL equals sanitation loan arm. Standard errors clustered at the village level are shown in round parentheses. *, **, *** indicate significance at the 10, 5 and 1 percent level, referring to Romano-Wolf p-values. These are obtained from a step-down procedure to adjust for multiple hypothesis testing performing 1000 bootstrap replications as proposed by Romano and Wolf (2005). Covariates: Toilet ownership at baseline, indicator for presence of a child aged 0 - 2 at baseline, ratio of number of sampled clients to village size. Amounts are in Indian Rupees (1 USD = Rs. 67.5). Data source: household survey.

Taking the null result on overall borrowing, combined with the finding that sanitation loans were taken up and every second one used to construct a new toilet, suggests that other investments (or consumption expenditures) must have been forgone as a result. While insignificant, coefficient estimates in columns 3-5 are supportive of this conclusion, suggesting a potential shift away from formal non-MFI borrowing as well as informal borrowing. The only positive coefficient observed, while also insignificant, is on MFI borrowing.

# **6.3.2 MFI borrowing**

We are able to use credit bureau data to look in more detail at micro-finance borrowing, with a more accurate measure compared to the household survey data. The data covers lending from all MFI providers in our study area over the study period. Table 11 considers impact estimates on total MFI borrowing (column (1)), borrowing from our implementing partner (column (2)) and borrowing from any other MFI (column (3)).<sup>49</sup> While we again find no significant impacts, the positive coefficients are in line with the previous evidence that the sanitation loan does not seem to have induced clients to
tion, net employment change, gross job reallocation, and the Herfindahl–Hirschman index (HHI)<sup>16</sup> ; and the independent variable of interest is the industry-level concentration of BOS, measured as the fraction of employment in BOS relative to total industry employment. To control for industry-level factors affecting firm dynamics, we include the average firm size - measured by employment - and age in year _t −_ 1, employment share, and lastly sector and year fixed effects. Because of the sharp effects of the Covid-19 pandemic on firm dynamics, we exclude 2020 from our analysis, and instead focus on the period from 2016 to 2019.

Table 15 presents the baseline estimation results at the 2-digit industry level for the nine measures of business dynamism. We find that a higher concentration of BOS in industrylevel employment is associated with lower employment share of young firms and increased market concentration as measured by the HHI, consistent with lower levels of business dynamism. On the other hand, we find that the share of employment in BOS is also related with higher job creation and lower job destruction, which result in net positive effect over employment change. However, their similar magnitudes result in an overall effect on job reallocation that is not statistically different from zero. Moreover, we do not find evidence that the concentration of BOS either encourages or discourages firm entry, and exit rates are not statistically different from other industries with lower presence of state businesses. In Table 16, we show that our results are consistent when estimated at a more disaggregated industry classification at the 3-digit level.

Finally, we perform one last robustness check by restricting the sample to competitive industries at the 2-digit level. Table 17 reports that all of the results described previously - considering the entirety of the economy - persist. Additionally, we find a statistically significant negative correlation between exit rates and the concentration of BOS in competitive industries. Our results suggest that industries with a higher presence of BOS are characterized by lower shares of young firms, lower levels
look at the joint impact of passport costs and restrictions, but instead regress migrants per capita on per capita income, the log of population, and the government effectiveness measure which was a prime determinant of passport costs. In Column 2 we also check how sensitive the results are to adding a squared term in per capita income and

> 13 Gender disaggregated migration data is not available at a sufficient level of detail to permit testing whether these restrictions have a greater effect on female migration, as one would expect.

- 18 -
interpret scores relative to the national norm. It also explains why mean _z_ -scores tend to be negative in our estimation sample.

Although our primary interest is the population of schools and students eligible for the program, nonrandom sorting of students into public and private schools in response to the scholarship may bias results. Such sorting is also an interesting potential outcome to investigate. In 2004, when program rollout was complete, only two of 43 districts had both a public and private high school (grades 10–12). By 2012, the last year for which we have data, this figure had grown to nine. We will therefore assess whether the growth in private school enrollment was related to the scholarship program.

However, all private schools are located in the urban districts of region 2, near the capital.<sup>9</sup> Students in most areas are therefore constrained to attend their local public school. We later check robustness of results to various definitions of the estimation sample, such as excluding region 2 or including private schools.

We also use data from the 1998 wave of the Integrated Household Survey (IHS) to explore heterogeneity in results by baseline characteristics. This survey, which is conducted by the Gambia Bureau of Statistics, is nationally representative and collects information on assets, demographics, and socioeconomic characteristics. In the 1998 survey, slightly over 1,900 households were covered including approximately 4,500 school-aged children. A third and final data set we use in the analysis is the annual school census conducted by the Ministry of Education, which spans the same years as the exam data. The Ministry reports enrollment by grade and gender for each school, and the number and gender of teachers.

Unfortunately, we are unable to link individuals across these three data sets, preventing us from connecting individual enrollment decisions or household characteristics with test results. We therefore use district and school characteristics to analyze treatment effect heterogeneity. At the district level, we construct three measures using the 1998 IHS. We
Q.E.D.

# **B Data Appendix**

Table 2 lists the countries in our sample and provides a brief description of the data sources.

The average size in the US manufacturing sector is read from the Business Dynamics Statistics database for the year 2007. As we did with the rest of the countries, we computed average firm size in the US and truncated the size distribution at ten workers or more.The data on the share of firms across two-digit manufacturing industries in the US stems from the County Business Patterns database, also for the year 2007.

## **B.1 Average Firm Size: Country-Specific versus Fixed Distribution of Firms across Sectors**

Figure 15 shows the extent to which controlling for cross-country differences in the distribution of firms across two-digit manufacturing industries affects the computation of the average firm size.

As the figure shows, for the majority of the countries, keeping the distribution of firms across two-digit industries fixed increases the average firm size. In other words, the US allocates more firms into higher average size industries compared to each country’s sectoral distribution, with the exceptions of Peru, Chile, and, more saliently, Kenya, which exhibits the opposite pattern. This result suggests that to account for the relative value of average size of each country with respect to the US, the model will require a higher level of entry barriers or a lower level of productivity-dependent idiosyncratic distortion. The figure also shows that, while important to accurately determine the relative magnitude of each type of distortion, controlling for production structures 61
of blackouts. Power outages were common in all the countries, and serious in Malawi (six out of every seven households reporting daily blackouts over the last 12 months), Niger, Nigeria, and Senegal.

Table 14: Summary of power blackout information

|Country|Findings|Quintile dependence|Urban vs. rural|
|---|---|---|---|
|Ethiopia|27% of households replying<br>reported no blackouts during<br>the last 7 days, but 24%<br>reported more than 3<br>blackouts. The number of<br>hours without electricity over<br>the last 7 days translated to<br>1.8 hours a day.|Both measures (no blackouts,<br>more than 3 blackouts)<br>decreased with increasing<br>quintile. The numbers of<br>hours without electricity did<br>not vary much with quintile.|20% of urban and 38% of rural<br>households reported no<br>blackouts, while 22% of urban<br>and 28% of rural households<br>reported more than 3<br>blackouts. The number of<br>hours per day without<br>electricity translated to 1.6<br>hours in urban and 2.3 hours<br>in rural areas.|
|Madagascar|The number of hours per day<br>electricity was available<br>averaged 19. 68% of<br>households replying reported<br>24‐hour availability.|Excluding the bottom two<br>quintiles, which had too few<br>samples, the number of hours<br>electricity was available per<br>day increased with quintile<br>nationally.|The number of hours<br>electricity was available per<br>day averaged 20 in urban and<br>18 in rural areas.
the Polity IV index of democracy does not appear as clear-cut in developing countries as some studies would have it (Xiaobo et al. 2018). With this caveat, and although it would be a stretch to interpret these studies causally, cross-national survey studies have provided an important basis and motivation for more (quasi-) experimental studies into the determinants of tax morale.

In observational studies, Pommerehne and Weck-Hannemann (1996) and Torgler (2005) show that Swiss cantons with more direct-democratic institutions also exhibit higher tax compliance. A similar implication is generated in the study by Alm and Torgler (2006) which finds that Switzerland and the U.S. have both strong direct democratic institutions and among the highest levels of tax compliance internationally. Much of the experimental work in this area has focused on laboratory settings, where many aspects of the environment are controlled by the researcher and the context and information environment can be manipulated more precisely. In one early landmark laboratory study Alm, Jackson, and McKee (1992) found that making decisions by voting increased tax compliance significantly in the lab. In their study of Swiss college students, Feld and Tyran (2002) argue that only notions of procedural legitimacy, which is generated by having laboratory subjects vote on a fine, can explain their finding that subjects comply more with a fine when it is voted on than when it is imposed. Importantly, while they do find a role for reciprocity (compliance with the fine is higher the more subjects voted for it) in explaining tax compliance, their argument goes beyond pure reciprocity to focus on _procedural fairness_ , or the belief that the method by which the decision was reached was fair.

More recently, Lamberton, De Neve, and Michael (2014) found evidence, also in a lab setting using American respondents, showing that simply allowing respondents to state their expenditure preferences reduced their use of a questionable tax loophole, thus raising compliance. They interpret this finding as reflecting a re-coupling of taxes with the services that they fund along the