rafmacalaba/datause-encoder-data huggingface dataset:
Appendix Table 6: ITT Treatment Effect Estimates, Short-Run Business Outcomes, Difference-inDifference OLS

|Outcome variable|ITT treatment<br>effect estimates|Control group<br>mean<br>(std. dev.)|
|---|---|---|
||(1)|(2)|
|Full-time paid employees|0.578|12.428|
||(2.351)|(22.281)|
||810|243|
|Avg. sales Dec 2008, Jan and Feb 2009 (1000s USD)|-14.464|63.384|
||(23.358)|(163.643)|
||675|200|
|Log (Avg. sales Dec 2008, Jan and Feb 2009 in 1000s USD)|0.017|2.391|
||(0.237)|(2.023)|
||675|200|
|Feb 2009 costs (1000s USD)|27.333|43.157|
||(25.419)|(113.758)|
||681|204|
|Profits (Feb 2009 sales minus costs, 1000s USD)|-15.357|11.460|
||(20.485)|(97.044)|
||602|176|
|Log (business assets)|-0.098|4.307|
||(0.227)|(1.699)|
||627|203|
|Productivity residual|0.306|-0.095|
|Residual from regression of log Feb 2009 sales|(0.217)|(1.272)|
|on log employees and log business assets|515|174|
|Return on assets (ROA)|0.272**|0.012|
|Feb 2009 sales minus costs divided by assets|(0.133)|(0.471)|
||488|154|

Note: Each cell in Column 1 contains the treatment effect point estimate, robust standard error, and number of observations, for a separate OLS difference-in-difference estimation. Each regressions uses the full sample of enterprises at baseline and follow-up and includes a dummy for being in the treatment group, a dummy for the follow-up period, an interaction term between the treatment and follow-up dummies, as well as controls for strata dummies, re-randomization variables, and a dummy for having been surveyed in March 2009 (vs. April, May or June) at follow-up. The point estimates displayed in Column 1 are coefficients on the interaction term between treatment and follow-up. Column 2 contains means and standard deviations for the control group at follow-up. Significance levels: *10 percent, **5 percent, ***1 percent.

36
**Table 1. Data Coding**

Cut off points are based on the examining data at end-June 2002 and in mid- November 20026:

||m|Q|**y**|
|---|---|---|---|
|1|3monthslag:2002/7|6monthslag:2002/3q|1yearlag:2001|
|2|6monthslag:2002/4|12monthslag:2001/3q|1.5yearlag:2000|
|3|withlongerlag|withlongerlag|longerlag|
|**4**|lowerfrequency, reas|onablyuptodate(2002/1|qforM,2001forQ)|
|5|lowerfrequency, longe|rlag||
|6|notavailablefromWD|I,IFS,or anyotherofficia|lwebsites|

For example, if I search for the CPI data in middle November 2002, and if the data are available for July 2002 or for more recent months, it is assigned a score of "1". If monthly data are available, not for July or later, but at least up to April 2002, then the score is "2". If the monthly data are only available for March 2002 or are even older, the score is "3". If the data are reported in lower frequency, for example, they are quarterly or annual and if the data are reasonably up to date (for data such as the CPI which are "desired" on a monthly basis, the requirement is that if it is reported as quarterly data, it should be available at least for the first quarter of 2002 or if annual data, then it needs to be available at least for the year 2001), then the score is "4". If the data are both produced at a lower frequency and is older than required a score of "4", or _"5"_ will be assigned. If the data are not available from any of the four sources (WDI, IFS, RMF or WB external websites or official websites of the countries), a "6" is assigned. The scores for each country on all indicators are averaged.

For GDP data, quarterly data are "desired", if the data are available for the first quarter of 2002 or for a more recent quarter, the country gets a score of "1" on this measure. If quarterly

> 6 Some additional countries were added in November 2002; the table is based on the observations in November.

8
# 3.1 Errors of representation

## <u>Hypothesis 1: Household sample selection effects</u>

In the absence of universal phone ownership in our study countries, it is possible that phone survey samples overrepresent certain population groups such as better-off and urban households (Ambel et al. 2021; Brubaker et al. 2021) . Similarly, non-response can lead to selective attrition from the sample, potentially affecting its representativeness for the general population. Even though our sampling strategy (collecting phone numbers from reference contacts) and re-weighting approach has been found to mitigate these issues, it is conceivable that some sample selection bias at the household level remains (Ambel et al. 2021; Gourlay et al. 2021) . If selection into our sample (either through coverage bias in the list of households with phone numbers or through non-response) is correlated with vaccine uptake, estimated coverage will be biased. We thus formulate the first hypothesis for the divergence between survey and administrative vaccine coverage estimates.

**Hypothesis 1:** Phone surveys overrepresent population groups that are more likely to be vaccinated.

The COVID-19 vaccination module implemented as part of the Ethiopia Socioeconomic Survey (ESS 5) gives us the opportunity to test this hypothesis. This module collected information on vaccine uptake for a nationally representative sample of households of which our phone survey sample is a subset. While sample selection effects may affect the phone survey sample, they should be mostly absent in a fully nationally representative sample. Therefore, we can compare estimated vaccine uptake among the sample of phone survey households (interviewed during the ESS 5) to estimated vaccine uptake within the whole, general population sample contained in the ESS 5. We formulate the following prediction.

**Prediction 1:** Households included in the phone survey will display higher rates of vaccine uptake compared to the general population in a nationally representative sample.

Empirically, we run the following OLS regression.

Where _Vis_ is a dummy for whether individual _i_ part of sample _s_ has been vaccinated with at least one jab of a COVID-19 vaccine. Subscript s denotes the sample to which individual _i_ belongs. All individuals are part of the general population sample whereas only some are living in households sampled for the phone survey. Some individuals will thus appear twice in the data, once in the phone sample and once in the general population sample. Our estimate of interest is _β,_ the coefficient on Di,s which is a dummy variable for whether observation _i,s_ is part of the phone survey sample. If our prediction is confirmed, _β_ should be statistically significant and positive.

9
<!-- Start of picture text --> 200<br>180<br>160<br>140<br>120<br>100<br>80<br>60<br>40<br>20<br>0<br>Return period: 1-in-20 1-in-100 1-in-500<br>44%<br>99%<br>94%<br>81%<br>61%<br>90%<br>79% 52% 28%<br>68% 46% 47% 56% 57%<br>Exposed rice production (hectares, thousands) 66% 69% 41% 29% 48% 38%<br>29% 50%<br>60% 55% 70% 13% 10% 13%<br>Quang Ninh Hai Phong City Thai Binh Nam Dinh Ninh Binh Thanh Hoa Nghe An Ha Tinh Quang Binh Quang Tri Thua Thien-Hue Da Nang City Quang Nam Quang Ngai Binh Dinh Phu Yen Khanh Hoa Ninh Thuan Binh Thuan Ba Ria-Vung Tau Ho Chi Minh City Tien Giang Ben Tre Tra Vinh Soc Trang Bac Lieu Ca Mau Kien Giang<br><!-- End of picture text --> Sources: Based on data from JAXA EORC 2018 (land use maps), Braese et al. 2020 (coastal flood data) and Fathom<sup>1</sup> (riverine flood data). Note: Shown percentages are percentages exposed rice area for a 1in500 year flood. A flood threshold of 25cm has been applied **.** The exposure of aquaculture production in the two big deltas is based on the two datasets of aquaculture ponds described in section 3.2, provided in vector format. In order to overlay these with flood maps, the pond datasets are converted into high-resolution raster data. This reduces the accuracy of the data, as ponds are not square and thus do not exactly match the raster grid. To increase robustness of the analysis, two different rasterization strategies are employed that yield an under and overestimation of the actual pond area.<sup>6</sup> The averaged result of the two strategies is used in further calculations. As the resolution of the flood maps is coarser than the ponds map, the impact of the information lost in the pond rasterization on the result is small. The remaining methodology for aquaculture exposure estimates is equivalent to that for agriculture. It involves downscaling of the flood raster, computing overlays per province, averaging the results from the two-pond rasterization strategies, and applying the flood extent offsets to account for flood protection infrastructure. This is repeated for all return periods in each of the two sets of flood maps – coastal and riverine – and each coastal province in the two deltas. The results for a 20-, 25-, 100- and 500-year return period are shown in figure 4.3.

22
that the high price of stopping and restarting public investment is taken into account. Finally, a third research suggestion is to widen the budgetary rule to include government consumption, which is kept constant in real terms in the present paper. To do this properly, the links between two key components of current government expenditures – social spending on education and health – and human capital will need to be defined and explored. The effectiveness of public service delivery in education and health is often hard to model by itself, let alone in a dynamic stochastic framework.

# **References**

Agénor, P. (2013). Public Capital, Growth and Welfare. New Jersey, Princeton University Press. Adjemian, S. and M. Juillard (2010) Dealing with ZLB in DSGE models: An application to the Japanese economy, ESRI Discussion Paper Series No.258

- Auty, R. M. (1993). Sustaining Development in Mineral Economies: The Resource Curse Thesis. London, Routledge.

- Arezki, R. and F. van der Ploeg (2008). “Can the Natural Resource Curse be Turned into a Blessing? Role of Trade Policy and Institutions.” IMF Working Paper 07/55 , Washington, International Monetary Fund.

- Berg, A., Portillo, R., Yang, S.-C. S., Zanna, L.-F., 2013. Public investment in resource-abundant developing countries. IMF Economic Review 61, 92–129.

- Berg, A., S. S. Yang, and L. Zanna (2014) Modeling African Economies: A DSGE Approach, IMF paper, Mimeo

- Benigno, G. and Fornaro, L. (2014), The Financial Resource Curse. The Scandinavian Journal of Economics, 116: 58–86

- Campbell, J. Y. and N.G. Mankiw (1989). “Consumption, Income, and Interest Rates: Reinterpreting the Time Series Evidence.” _NBER Macroeconomics Annual_ 6:141-201.

- Collier, P. and A. Hoeffler (2004). “Greed and Grievance in Civil War.” Oxford Economic Papers, Vol. 56, No.4, pp.563-95.

- Corden, M. and P. Neary (1982). “Booming Sector and De-Industrilization in a Small Open Economy.” Economic Journal, Vol. 92, pp. 825-48.

- Collier, Paul, Rick van der Ploeg, Michael Spence, and Anthony J. Venables. 2010. “Managing Resource Revenues in Developing Countries.” _IMF Staff Papers,_ Vol. 57, No. 1, pp. 84-118.

- Devarajan, S., D. Go, J. Page, S. Robinson and K. Thierfelder (2008). “Macroeconomic Dynamics of Scaling Up Foreign Aid.” Chapter 5 in D. Go and J. Page, eds., Africa at a Turning Point? Growth, Aid and External Shocks. The World Bank.

- Devarajan, S., D. Go, and H. Li (1999). “Quantifying the Fiscal Effects of Trade Reform.” World Bank Policy Research Working Paper #2162 (August).

- Devarajan, S. and D. Go (1998). “The Simplest Dynamic General Equilibrium Model of an Open Economy.” Journal of Policy Modeling (December). 20 (6):677-714.

- Dagher, J., J. Gottschalk, and R. Portillo (2010). “Oil Windfalls in Ghana: A DSGE Approach.” IMF Working Paper # WP/10/116. Washington, D.C.

30
rigidity, as suggested by the small magnitude of the estimated coefficients. In Uruguay, white collar workers are more likely to be subject to DNWR, in line with most of the models discussed in this section. In contrast, occupational dummies in the case of Brazil all have very small effects.

There is a strong negative association between establishment size and the probability of being subject to either form of rigidity. In Uruguay, the smallest establishments present a probability of being subject to DRWR (DRWR) that is 6.7pp (11pp) larger than the reference category (establishments with more than a 1,000 employees). In Brazil, size effects in the case of DNWR are of fairly small magnitude. In contrast, the likelihood that a worker’s wage is subject to DRWR in the lowest size group is about 6.5pp lower than if that worker is employed in one of the largest firms in the sample. This evidence appears to be against shirking models of efficiency wages, but is in line with estimates of DRWR in Belgium reported in Du Caju et al. (2007) and with the greater flexibility in compensation policies of larger firms found in surveys of wage setters in European firms (Babecký et al., 2009).

As expected, the wage level in the base year, as measured by the three wage quartile dummies, has little impact on the probability of being subject to DNWR. Perhaps surprisingly, however, we also find very little impact of the wage quartile dummies in the case of DRWR in Brazil, where a concentration of rigidity across low-earning individuals might have been expected, given the importance of the minimum wage. The main rationale for this result lies in the fact that some of the covariates included in the regression, most notably age, education, and occupation dummies, are capturing the wage level of workers. An unconditional regression of the incidence of DRWR on the quartile dummies yields a highly significant and sizable negative association: workers whose wage level is in the fourth quartile have a probability of being subject to DRWR that is 3.6pp lower than workers earning wages in the first quartile. If we concentrate on the pre-1999 sample, the period where the focal point of DRWR coincides with the growth of the minimum wage, this difference increases to 5.8pp. As before, similar unconditional regressions show no observable differences in DNWR across wage quartiles.

In the case of Brazil, we take advantage of the fact that we observe every formal 23
# **Table 7: Total Effects Margin on Time Use (weekly hours)**

## **SUR estimates, standard errors in parentheses**

||**Learning**|**IGA**<br>**Age**|**Chores**<br>**d 12-17**|**Leisure**<br>**at BL**|**ELA Club**|**Learning**|**IGA**<br>**Age**|**Chores**<br>**d 18-25**|**Leisure**<br>**at BL**|**ELA Club**|
|---|---|---|---|---|---|---|---|---|---|---|
||**(1)**|**(2)**|**(3)**|**(4)**|**(5)**|**(6)**|**(7)**|**(8)**|**(9)**|**(10)**|
|**Disruption Effect**|-12.2***|6.07**|5.62***|1.76|-|-2.50|-3.10|3.37*|2.56*|-|
||(2.37)|(3.10)|(1.89)|(1.63)||(1.54)|(2.50)|(1.87)|(1.55)||
|**Treatment Effect in High Disruption**|9.84***|-2.35|-4.68**|-4.70***|3.02***|2.42*|3.03|-3.09*|-4.08***|2.83***|
||(2.62)|(3.26)|(1.91)|(1.51)|(.265)|(1.41)|(2.49)|(1.74)|(1.42)|(.252)|
|**Treatment Effect in Low Disruption**|-3.03**|1.72|.480|-2.77***|3.19***|-.978|1.46|.325|-2.97***|2.74***|
||(1.30)|(1.20)|(.790)|(.810)|(.157)|(.931)|(1.84)|(1.18)|(.868)|(.145)|
|**Difference [β3, p-value]**|{.000}|{.239}|{.012}|{.262}|{.528}|{.051}|{.613}|{.114}|{.510}|{.741}|
|**Control Mean at BL**|48.8|15.1|42.3|26.4|-|8.02|32.5|59.6|30.9|-|
|**Observations**|2,381|2,381|2,381|2,381|2,381|2,400|2,400|2,400|2,400|2,400|

**Notes:** ***, ** and * denote significance at the 1%, 5%, and 10% levels. Time allocation data was collected both at Baseline and Endline. Respondents were provided a set of 25 beads and a board with 6 circles representing: "Learning Activities", "IGA", "Leisure", "Household Chores", "Sleep" and "Other". The Learning category includes schooling, vocational training and study time. "IGA" includes paid and unpaid work of any kind. Respondent were then asked to allocate beads into each circle in a way that represents time allocation in an average day, and data points were later converted into weekly hours. The main results are estimated with an ANCOVA specification where the estimated SUR system includes six time allocation variables, the "Other Time Use" category is not reported. Control variables include: age, PPI score, household size, illiteracy, village size (nr of dwellings), village average PPI score, distances form key facilities (clinic, secondary school and market), a dummy equal to one if the village is a political stronghold (i.e. has a resident paramount and/or section chief), the number of NGOs active within the village before the Ebola outbreak (excluding BRAC), share of Christian households, distance from Freetown and distance from Kailahun. All specifications include dummies for the randomization strata (district) and errors are clustered at the unit of randomization (village).
non-linear.<sup>3</sup> We use data from the Nepal Living Standard Survey (NLSS) of 1995/96 to uncover the role played by the extent of the market in agricultural specialization and commercialization at the village level. Crop agriculture in Nepal, like many other developing economies, is characterized by low degree of commercialization and specialization on average. There are, however, striking di ff erences among villages in terms of the level of agricultural development covering the entire range from completely specialized production of non-staple crops to nearly complete subsistence agriculture. The stark geographical di ff erences in Nepal also resulted in large variation in sizes of the urban centers (from population of 10,000 in smaller towns to 421,000 in the capital city Kathmandu in 1991). These large variations in the level of agricultural development along with that in access to and size of urban markets enable us to empirically characterize the relationship between agricultural specialization and the extent of the market. The results based on the Nepalese data are, however, of more general interest as they are likely to be applicable to many other developing countries which are characterized by relative isolation of rural areas due to poor infrastructure as well as low level of agricultural development.<sup>4</sup> We analyze two dimensions of structural change: the pattern of product diversi fi cation (crop specialization), and the degree of market production as opposed to home production (i.e., commercialization of agriculture). The pattern of crop specialization is measured by Her fi ndahl index of concentration of cropland use, and by the share of land devoted to noncereal crops. Sales of non-rice crops and all crops as a percentage of total production are taken as measures of commercialization. Empirical estimation of this paper introduces several improvements. First, as opposed to the standard practice of de fi ning market as the nearest urban center, we allow for the possibility that villagers may be trading at multiple urban centers. We de fi ne the extent of the market as an average of the gravity measures of all the markets where villagers may trade. The gravity measure itself is de fi ned as a ratio of urban

> 3 For an interesting theoretical analysis that highlights the tension between the increasing returns and risk in determining technological change and production structure in agriculture, see Dixit, 1993.

> 4 These would include regions like Northern India and Pakistan, and many other developing countries in Africa and Asia.

3
typically primary earners in Kenya, I consider only the oldest two cohorts of men for this analysis, so that the incapacitation effect of continued schooling does not dominate the patterns of interest.<sup>36</sup> According to 2008 Demographic and Health Survey (DHS) data, young men in Kenya without secondary school have a higher employment rate at age 20 than do men who complete secondary school, since the latter group has had less time to look for jobs. At roughly age 25 (the mean age of the older two male KLPS2 cohorts), DHS data show roughly equal employment rates in these two groups; as they grow older still, the better educated are more likely to be employed. I confirm exactly this pattern in KLPS2, shown in Panel A of Table 4, columns 1 and 2. OLS shows a fairly precise zero effect of secondary schooling on employment at this age. However, the regression discontinuity approach gives very different results: the coefficient on schooling is positive and significant depending on controls, shown in IV probit and bivariate probit specifications in columns 3-6. While 2SLS is positively signed, it is insignificant; this is in part because 2SLS is less efficient than estimation via IV probit and bivariate probit when the true model is nonlinear and the mean of the response variable is close to zero or one, as in this case.<sup>37</sup> Depending on the specification, I find a rise in employment of between 24 and 43 percent in response to secondary schooling.

Besides being employed by someone outside their family, many respon-

> 36As shown in Panel C of Table 1, only 13 percent of the men in the oldest two cohorts are still in school, as compared to 44 percent in the younger four cohorts. Human capital effects of secondary school remain broadly similar when limiting the sample to respondents who were in standards 6 and 7 in 1998, though standard errors widen (predictably) with the lower sample size; results shown in Panel B of Table 3.

> 37As a diagnostic, predicted values from 2SLS clearly lie outside the unit interval.

23