rafmacalaba/datause-encoder-data huggingface dataset:
# **E.23 Calculating Reduction in** _R_ 0

_R_ 0 is the reproduction rate of a disease: the average number of secondary cases generated by the average infectious individual. To calculate the implied reduction in _R_ 0 due to our treatments we follow the approach of Pronyk et al. (2016), which the authors detail in their online appendix.<sup>A13</sup> _R_ 0 is calculated by multiplying the disease transmission rate by the average duration of infectiousness, _D ≥_ 0. The duration of infectiousness is time during which an infected patient can spread disease.

We adopt Pronyk et al.’s (2016) assumption that transmission rates do not change following public health interventions (in their case the construction of Community Care Centers). Conditional on a infected individual and susceptible individual coming into contact, the likelihood that Ebola is transmitted between the two is unaffected by treatment. Granting this assumption, treatment can affect _R_ 0 by changing _D_ ( _T_ ), which is calculated as follows: where _t_ ( _T_ ) is the time between symptom onset and isolation among individuals who are isolated; _r_ ( _T_ ), the proportion of individuals who are isolated; and _T_ is a binary treatment indicator. If an individual does not report, Pronyk et al. (2016) assume they remain infectious for 10 days.

The average time between symptom onset and reporting — _<u>t</u>_ <u>(</u> _T_ = 1) and _<u>t</u>_ <u>(</u> _T_ = 0) — can be calculated from data. In our sample, _<u>t</u>_ <u>(</u> _T_ = 0) = 4 _._ 73 and _<u>t</u>_ <u>(</u> _T_ = 1) = 4 _._ 97; we cannot reject the null that these are equal (see Table E.5).

Pronyk et al. (2016) assume a baseline reporting rate of 50 percent from mid-November to January, which is also the period that the disease was a major threat in our study area. 50 percent is consistent with other estimates, though it may understate the extent of under-reporting; the CDC’s initial estimate was 40 percent.<sup>A14</sup> Going forward, assume _r_ ( _T_ = 0) = 0 _._ 5 and _r_ ( _T_ = 1) = _r_ ( _T_ = 0) _· τ_ .

Assuming the (initial) stock of Ebola cases is balanced across treatment and control, then _τ_ = _y_ ( _T_ = 1) _/y_ ( _T_ = 0), where _y_ ( _T_ ) is the number of reported cases and can be calculated from our data. Our estimates in Table 3 imply that � _τ_ = (0 _._ 281 + 0 _._ 173) _/_ (0 _._ 281) = 1 _._ 62.

With these quantities in hand, we can calculate _D_ ( _T_ ): This implies that treatment generated a 19 percent reduction in _R_ 0. Pronyk et al. (2016) estimate that CCCs contributed to a 13–32 percent reduction in _R_ 0.<sup>A15</sup>

> A13 `https://ajph.aphapublications.org/doi/suppl/10.2105/AJPH.2015.303020/suppl_file/web+appendix+ r2.docx`

> A14 `https://stacks.cdc.gov/view/cdc/24901`

> A15 Their estimate is likely conservative, as they do not incorporate how Community Care Centers affect reporting rates.

A65
Policy Research Working Paper 6772

# **Abstract**

Over the past decade the international community, especially the World Bank, has conducted programs to increase local public service delivery in developing countries by improving local governing institutions and creating social capital. This paper evaluates one such program in Sudan to answer the question: Can the international community change the grassroots civic culture of developing countries to increase social capital? The paper offers three contributions. First, it uses lab-in-the-field measures to focus on the effects of the program on pro-social preferences without the confounding influence of any program- induced changes on local governing institutions. Second, it tests whether the program led to denser social networks in recipient communities. Based on these two measures, the effect of the program was a precisely estimated zero. However, in a retrospective survey, respondents from program communities characterized their behavior as being more pro-social and their communities more socially cohesive. This leads to a third contribution of the paper: it provides evidence for the hypothesis, stated by several scholars in the literature, that retrospective survey measures of social capital over biased evidence of a positive effect of these programs. Regardless of one’s faith in retrospective self-reported survey measures, the results clearly point to zero impact of the program on pro-social preferences and social network density. Therefore, if the increase in self-reported behaviors is accurate, it must be because of social sanctions that enforce compliance with prosocial norms through mechanisms other than the social networks that were measured.

This paper is a product of the Social Protection Unit, Africa Region; and Impact Evaluation Team, Development Research Group. It is part of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy discussions around the world. Policy Research Working Papers are also posted on the Web at http:// econ.worldbank.org. The authors may be contacted at aavdeenko@diw.de and michael.gillian@nyu.edu.

_The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent._ Produced by the Research Support Team
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# Tableof ContertAJ

# Executive summary

# List of tables

# List of acronyms

|1.|Methodology|2|
|---|---|---|
|II.|Unit costs|7|
|111.|<br>Cost structure|12|
|IV.|Cost-effectiveness|16|
|V.|Financing|18|
|VI.<br>App|Summary<br>endices:|22|
|A.|Summary of main interventions in Chile|44|
|B.|Summary of main interventions in Philippines|50|
|C.|Summary of main interventions in Malawi|59|
|D.|List of contacts|62|

# Bibliography

63
Fasani, F and J Mazza. 2020b., “Being on the Frontline? Immigrant Workers in Europe and the <u>COVID-19 Pandemic,”</u> _IZA_ Discussion Papers 13963.

Friedberg, Rachel M. 2000. “You can’t take it with you? Immigrant assimilation and the portability of human capital,” _Journal of Labor Economics_ , 18(2): 221–51.

Foged, Mette and Giovanni Peri. 2016. “Immigrants' Effect on Native Workers: New Analysis on Longitudinal Data,” _American Economic Journal: Applied Economics_ , 8 (2): 1-34.

Garrote Sanchez, Daniel, Nicolas Gomez Parra, Caglar Ozden, and Bob Rijkers. 2020. “Which jobs are most vulnerable to COVID-19? Analysis of the European Union,” _World Bank Research & Policy Briefs_ No. 34. Washington, D.C.: World Bank Group _._ Giuntella, Osea, and Fabrizio Mazzonna. 2015. “Do immigrants improve the health of natives?” _Journal of Health Economics_ 43: 140–53.

Goel, Deepti, and Kevin Lang. 2017. “Social Ties and the Job Search of Recent Immigrants,” _ILR Review_ .

Green, David A. 1999. “Immigrant Occupational Attainment: Assimilation and Mobility over Time,” _Journal of Labor Economics_ 17 (1): 49-79.

Hao, Lingxin. 2008. “Workplace Nonfatal Injuries Among Immigrants to the U.S.” Mimeo, Johns Hopkins University Department of Sociology. Available online at <u>http://paa2008.princeton.edu/download.aspx?submissionId=80386.</u> Hersch, Joni, and W. Kip Viscusi. 2010. “Immigrant Status and the Value of Statistical Life.” _Journal of Human Resources_ 45 (Summer): 749-771.

Hildebrandt, Nicole, and David J. McKenzie. 2005. “The Effects of Migration on Child Health in Mexico.” _Economia_ 6 (1): 257–89.

Juranek, Steffen, Jörg Paetzold, Hannes Winner, and Floris Zoutman. 2020. “Labor market effects of COVID-19 in Sweden and its neighbors: Evidence from novel administrative data.” NHH Dept. of Business and Management Science Discussion Paper 2020/8.

<mark>Khamis, Melanie, Daniel Prinz, David Newhouse, Amparo Palacios-Lopez, Utz Pape, Michael Weber. 2021. “The Early Labor Market Impacts of COVID-19 in Developing Countries: Evidence from High-Frequency Phone Surveys.” Policy Research Working Paper No. 9510. World Bank, Washington, DC. © World Bank.</mark> Kramarz, Francis and Oskar Nordström Skans. 2014. “When Strong Ties are Strong: Networks and Youth Labour Market Entry,” _Review of Economic Studies_ , 81 (3): 1164–1200.

<mark>Kugler, Maurice; Mariana Viollaz, Daniel Duque, Isis Gaddis, David Newhouse, Amparo Palacios-Lopez, Michael Weber. 2021. “How Did the COVID-19 Crisis Affect Different Types of Workers in the Developing World?” Jobs Working Paper No. 60. World Bank, Washington, DC. © World Bank.</mark> 30
Figure 3.2. Growth Incidence Curve for Indonesia: 1996-2002 <!-- Start of picture text --> 30<br>20<br>10<br>1999-200 2<br>0<br>1996-1999<br>-10<br>-20<br>-30<br>-40<br>0 10 20 30 40 50 60 70 80 90 100<br><!-- End of picture text --> Cumulative Percentage of Population The reduction in poverty experienced by the country between 1993 and 1996 is in fact part of a trend that started in the mid 1980s. Over that period of time, the country successfully adjusted to the oil price shock, the overheating of the economy early in the 1990s, and raised domestic interest rates to protect the rupiah against the contagion effect of the 1995 Mexican crisis (World Bank 1995 and 1996). The induced macroeconomic stability and a well-functioning labor market provided a good foundation to sustained economic growth over the 1984-1996 period, which ultimately led to significant gains in household welfare. The mean per capita monthly expenditure increased in real terms by 17
- 19 -

and travel distance and increase with the difference in elevation, which is consistent with the above estimation without the fixed effects.

37. One distinct outcome may be that the coefficient associated with driving speed turned out to be positive, not negative, or statistically insignificant. First, it means that there must be unobservable carrier-specific characteristics that systematically affect driving speed, such as fleet age, other technical vehicle attributes and carriers’ driving behavior.

38. Second, there is a possibility that the effect of speed or transport efficiency may be heterogeneous across different types of commodities, thus, offsetting the impact. To examine this possibility, the fixed-effects regression is separately performed for each of the subgroups. It is found that the impact of driving speed is negative and significant for food and other consumer goods ( **Table 7** ). The freight costs for these commodities seem to be particularly sensitive to transport efficiency. For other merchandises, driving speed may not matter.

**<u>Table 5. Freight carrier fixed effects model</u>**

||Linear||Quadratic||Logarithm|ic|
|---|---|---|---|---|---|---|
||Coef.|Std.Err.|Coef.|Std.Err.|Coef.|Std.Err.|
|_speed_|0.002|<br>(0.001) **|3.3E-04|(4.0E-03)|||
|_speed_<sup>2</sup>|||9.5E-06|(4.2E-05)|||
|ln_speed_|||||-0.014|(0.009)|
|_dist_|-1.7E-03|(5.9E-05) ***|-1.8E-03|(1.4E-04) ***|||
|_dist_<sup>2</sup>|||3.0E-07|(3.0E-07)|||
|ln_dist_|||||-0.050|(0.002) ***|
|_elev_|1.1E-03|(2.4E-05) ***|2.3E-03|(5.4E-05) ***|||
|_elev_<sup>2</sup>|||-2.2E-06|(7.7E-08) ***|||
|ln_elev_|||||0.050|(0.001) ***|
|_D_elev_|||||-0.239|(0.033) ***|
|_crossborder_|0.192|<br>(0.008) ***|0.172|(0.008) ***|0.037|(0.002) ***|
|constant|3.123|<br>(0.042)***|3.070|(0.097)***|1.214|(0.037)***|
|Obs.|51,137||51,137||51,137||
|R-squared|0.947||0.9479||0.8857||
|F stat.|...||...||...||
|No. of carrier dummy<br>variables|8952||8952||8952||

Note: The dependent variable is freight rate, _p_ . for the first two models, and the log of freight rate, ln _p_ , for the last column model. Robust standard errors are shown in parentheses. *, ** and *** indicate statistical significance at the 10, 5 and 1 percent level, respectively.
where ln( _ych_ ) is log of per capita expenditure of household _h_ in cluster _c_ , _X ch_ the vector of the common variables, β the vector of regression coefficients, η _c_ the cluster-specific random effect and ε _ch_ the household-specific random effect. The subscript _ch_ refers to household _h_ living in cluster _c_ . We estimate different models for the six regions separately, to allow for variation in the relationship between expenditure and the selected variables in these areas. Table 1 in the Appendix lists the selected variables that are included in the regression models, i.e. selected on the basis of being common to both the survey and census and contributing significant explanatory power.

In the third step, we predict expenditure of a household in the census as follows: ˆ ˆ where β<sup>ˆ</sup> , η _c_ and ε _ch_ denote the estimates for β , η _c_ and ε _ch_ . The predicted expenditure is used to calculate the poverty rate of small areas. It should be noted that the point estimates as well as the standard errors of the poverty rate and per capita expenditure are calculated by ˆ ˆ Monte-Carlo simulations. In each simulation, a set of values β<sup>ˆ</sup> , η _c_ and ε _ch_ are drawn from their estimated distributions, and an estimate of expenditure and the poverty rates are obtained. After _k_ simulations, we can obtain average expenditure and its standard deviation over the _k_ different simulated values. Since we are restricted to a 15% sample of the 2009 Population Census (as opposed to the full census), we add an additional sample error component to the standard deviation. For this, we in effect treated the census as a survey, taking account its complex design and sample weights.

The predicted expenditure for all households in the population census are subsequently aggregated to generate district- and province level welfare measures. In 2009, we apply the GSO-World Bank official poverty line of 7,836,000 VND/person/year, and in 1999 the line is 1,789,871 VND/person/year (Minot et al, 2003). As poverty measure we use the popular headcount rate. We also estimate the Gini coefficient as our primary indicator of income inequality at the local level.

6
**TABLE 10: Impacts on Parenting Quality - 36-Month Follow-Up**

|||**Stimulati**|**on Index**<br>**Dependen**|**Positive**<br>**In**<br>**t variable:**|**Practices**<br>**dex**|
|---|---|---|---|---|---|
|**Variables**||**(1)**|**(2)**|**(3)**|**(4)**|
|T2 (careiver trainin)||-0.045|-0.036|-0.051|-0.064|
|g g||(0.076)|(0.073)|(0.071)|(0.072)|
|T3 T2 + i iti||0.062|0.061|0.002|-0.013|
|( caregver ncenves)||(0.082)|(0.081)|(0.067)|(0.068)|
|T4 T2 + i ii||0.172**|0.164**|-0.067|-0.071|
|( parentng tranng)||(0.082)|(0.077)|(0.067)|(0.067)|
|Lagged Dependent Variable (Baseline)|||0.207***<br>(0.030)||0.110***<br>(0.032)|
||T2=T3|0.138|0.180|0.454|0.444|
|F-test for Equality of Parameters - p-value|T2=T4|0.003***|0.005***|0.821|0.917|
||T3=T4|0.150|0.186|0.315|0.379|
|District-bin FixedEffects?||Yes|Yes|Yes|Yes|
|Lagged Dependent Variable and Age Dummies?||No|Yes|No|Yes|
|Number of observations||2,033|2,033|2,030|2,030|

Notes: .01 - ***; .05 - **; .1 - *; OLS regressions at the child level using baseline and 36-month data on Stimulation and Positive Practices. Standard errors in parentheses are clustered at the CBCC level. We use all children for whom the dependent variable is available for the 36-Month Follow-Up. Even columns control for the baseline value of the dependent variable. We weight observations using sampling weights. For each round, indices are stardardized using the (weighted) mean and standard deviation for the control group in that round.

53
# **Could the Debate Be Over?**

**Errors in Farmer-Reported Production and Their Implications for the Inverse Scale-Productivity Relationship in Uganda**

Sydney Gourlay<sup>‡</sup> , Talip Kilic<sup>†</sup> , and David Lobell<sup>#1</sup> <mark>JEL Codes: C23, C83, Q12.</mark> <mark>Keywords: Maize, Yield Measurement, Plot Area Measurement, Inverse Scale-Productivity Relationship, Crop Cutting, Remote Sensing, Household Surveys, Uganda, Sub-Saharan Africa.</mark> 1 The senior authorship is shared between Sydney Gourlay and Talip Kilic. ‡ Corresponding author. Ph.D. Candidate, Department of Economics, The American University, Washington, DC, and Survey Specialist, Living Standards Measurement Study (LSMS), Survey Unit, Development Data Group, World Bank. <u>sgourlay@worldbank.org</u><sup>†</sup> Senior Economist, Living Standards Measurement Study (LSMS), Survey Unit, Development Data Group, World Bank, Rome, Italy. tkilic@worldbank.org.<sup>#</sup> Professor, Center on Food Security and the Environment, Stanford University, Stanford, CA. <u>dlobell@stanford.edu. The authors would like to thank for their comments (in alphabetical order) Leigh</u> Anderson, Leah Bevis, Sam Desiere, Nancy McCarthy, the participants of (i) the USAID Uganda Agriculture Market Systems Workshop (March 2017, Kampala, Uganda), (ii) the World Bank Land and Poverty Conference (March 2017, Washington, DC), (iii) the Centre for the Study of African Economies (CSAE) conference (March 2017, Oxford, UK); (iv) the FAO Agricultural Development Economics Seminar and the IFAD Research and Impact Assessment Seminar (April 2017, Rome, Italy), (v) the University of Copenhagen Development Economics Seminar (May 2017, Copenhagen, Denmark), and (vi) the XV EAAE Congress (August 2017, Parma, Italy).
the two waves of the survey (Figure 6, panel b). However, this still represents a large share (32%) of the firms that make downward adjustments on the intensive margin. Employment changes are especially rampant for firms that already adjusted in wave 1. Of the firms that made a downward shift in employment on both the intensive and extensive margins in wave 1, 60% continue to adjust on either margins. Moreover, 25% of firms that did not modify employment during wave 1 are also adjusting, albeit mainly on the intensive margin (Table 1).

Figure 6: Evolving employment adjustments during the pandemic <!-- Start of picture text --> (a) Extensive margin (b) Intensive margin<br>20 60<br>16<br>15 14 44<br>40<br>32<br>10<br>20<br>5<br>0 0<br>Wave 1 Wave 2 Wave 1 Wave 2<br>Probability of having fired empl. Probability of intensive adjustment<br><!-- End of picture text --> Table 1: Transition in employment adjustment patterns across waves

||||**Wa**|**ve 2**||
|---|---|---|---|---|---|
|||No employment<br>changes|Extensive<br>margin only|Intensive<br>margin only|Extensive and<br>intensive margins|
||No employment changes|74.5|17.7|2.9|4.8|
|**Wave 1**|Extensive margin only|61.3|15.2|7.7|15.8|
||Intensive margin only|50.3|37.7|6.5|5.5|
||Extensive and intensive margins|37.9|32.5|18.3|11.4|

# **4.3 Stylized Fact 3: The recovery among firms is heterogeneous and more sensitive to firm-level attributes rather than to country-level differences in the severity of the initial shock.**

The analysis of firm outcomes, focusing on average trends, masks significant heterogeneity in performance. Such heterogeneity is well-noted in many studies, including the one using the first wave of BPS (Apedo-Amah et al., 2020). The second wave of BPS data allows us to explore the heterogeneity in recovery process within and across countries.

_First_ , firms in countries with more severe initial shock (as measured by the drop in mobility drop) are catching up in performance relative to their peers in countries facing a lower severity of the shock. For instance, while firms in countries with more severe mobility drop during the start of the pandemic witness a decrease in sales by 49% in wave 1 and 29% in wave 2, those in countries with milder disruptions in mobility observed a decline in sales by 39% during wave 1 and 28% in wave 2 (Figure 7, panel a). A similar pattern is also found with the probability of being open (Figure 7, panel b).

14
At the end of the endline survey, there was approximately equal representation between the treatment (750) and control (757) groups, with 394 and 391 fewer observations from each group respectively. This was despite ongoing conflict keeping enumerators from going to a few counties due to insecurity.<sup>6</sup> As a robustness check on results, the difficult‐to‐reach study participants (those reached only through intensive tracking) are reweighted to regenerate the baseline sample. This recognizes that the hard‐to‐reach may be more representative of the outstanding missing observations in the endline data than those reachable through the phone survey.

The main approach for measuring outcome variables was through face‐to‐face interviews that were conducted as part of baseline and endline surveys described above. In addition, risk preferences, trust attitudes and engagement in crime and violence were assessed using experimental data collected during these face‐to‐face interviews from decisions reported over lotteries, trust games and elicited through list experiments (see appendix 1 for full methodological details).

The hypotheses of this study are grouped into 2 main families of outcomes – socio‐economic outcomes, and psychological and behavioral outcomes. It is possible that these families of outcomes were differently affected by the intervention. For instance, it is possible that participants who failed to access the grant but participated in the training did not experience any negative effects on their socio‐ economic situation while suffering negative effects on their psychological and behavioral well‐being. Table 1 Main outcomes of interest provides detailed information on the individual outcomes we studied in each category.

# 4. Methodology

# 4.1 Selection into treatment arms

Selection into treatment arms was a two‐stage process. In the first stage participants from the control group and the original treatment group were randomly selected according to the originally planned experiment. A balance test on these baseline study participants shows no systematic differences between the original control and the treatment groups (Table2). We find weak evidence that the control group was slightly less affected by the conflict. Our measure of conflict exposure is based on geo‐referenced data by UCDP (Sundberg and Melander 2013). It consists in an average of deaths by event within a 300 km radius weighted by geographic proximity to participants’ baseline location.<sup>7</sup>

> 6 In WEQ: Mvolo, Mundri East, and Mundri West ; in CEQ: Kajo Keji, Morobo, and Lainya ; in Lakes: Rumbek North (flooding during time of data collection).

> 7 300 km equals the maximum distance of any program participants to a KCB bank branch. We also tested 50 km, 100 km, 200 km radii, but the results remain extremely similar.

9