rafmacalaba/data-use-mentions-extended huggingface dataset:
impact) on entry behavior. With only cross-sectional data, one would be forced to deal with this fact by including as many agglomeration attributes in the model as possible. While such data exist, they will necessarily be incomplete. With our panel data (obtained by using annual entry behavior observed in the RAIS), we are able to control nonparametrically for any features of each agglomeration that do not change over time. This takes care of the most important differences between agglomerations, and leaves us with the variation in CF allocations over time with which to identify their impact.

# **_Stage #3:   Decomposing Agglomeration Fixed Effects_**

In the final stage of our estimation procedure, we explore the role of determinants of entry behavior besides the CF’s. At the end of Stage #2, we are left with the vector of agglomeration-and-industry fixed effects, φ _m_ . These fixed effects describe the attractiveness of each agglomeration for each industry _m_ , averaged over the period 19932001, after having controlled for headquarter locations, time effects, and CF allocations. Ideally, we could take these fixed effects and regress them on a vector of city attributes; e.g., _Xj_ = {IDH, education, infrastructure, employment in sector _m_ (i.e., agglomeration effects), employment in other sectors (i.e., spillover effects)}. In practice, this is complicated by two factors. First, many of these attributes are highly correlated with one another (see Table 4). Results of such a procedure are therefore highly sensitive to the exact specification assumed. Second, it is likely that some of these attributes are actually determined by the entry behavior of firms, and are therefore endogenous to the regression. This is especially true of the aggregated entry decisions of other firms. In this case, a simple decomposition like that described above would yield biased estimates.

18
set of dummy variables for the 8 main Indonesian islands (groups)<sup>30</sup> that the district is located on, and ε���� captures all other unobserved nominal wage determinants.

Finally, S�� denotes our main independent variable of interest. In our main specification, we follow De la Roca and Puga (2017) in the specification of this variable. For all districts that belong to a metro area, it is defined as “ _the number of people living within 10 km of the average person in the metropolitan area, m, to which district, d, belongs_ ”, i.e. it takes the same value for all districts belonging to the same metro area. For all districts that do not belong to a metro area, it is defined as _“the number of people living within 10 km of the average person in the district, d”_ . Crucially, this variable varies depending on the algorithm/approach used to define metro areas. We use this variable instead of a simpler density measure, as it is (see De la Roca and Puga, 2017, p.112) better able to deal with the noise introduced by urban boundaries that vary across urban areas in their tightness around built-up areas. We calculate this variable using the same _Landscan_ - _2012_ gridded population data that we used to define metro areas using the AI and cluster algorithms (see Section 3.1 above).

27 SAKERNAS reports monthly income for sampled individuals. Based on this, and a person’s reported total working hours during the last week, we calculate his/her hourly wage as: (monthly income / (365/12))  (7/hours worked last week). SAKERNAS reports both monthly income earned in cash as well as in goods. In all results reported here, we use total monthly income, i.e. total monthly income in cash and in goods combined. All our findings are robust to using only
# **1. Introduction**

The impact of the global coronavirus pandemic (COVID-19) was felt by the entire world, but not everyone was affected equally. The pandemic led to the largest global economic crisis since the Great Depression, with 95 percent of countries experiencing a contraction in output in 2020. It is estimated that the pandemic and the associated economic recession have led to an additional 97 million people in extreme poverty in 2020, resulting in the first increase in global poverty in nearly a quarter century (World Bank, 2020). This puts the Sustainable Development Goal of reducing global extreme poverty to 3 percent further out of reach. The actual impact of the pandemic on poverty may eventually be considerably more severe than this early estimate since it assumes that the pandemic has not increased inequality. For example, even a small increase (by one percentage point) in the Gini index of inequality<sup>2</sup> in every country could have increased the global poverty impact of the pandemic by around 35 percent in 2020 (Lakner et al, forthcoming).

As the pandemic is still unfolding, the degree to which its effects are dis-equalizing will not be known for some time, and they will also depend on the nature of inequalities that are being considered. For instance, Deaton (2021) shows that economic contractions, measured in terms of GDP per capita, were larger in richer countries, resulting in a reduction of unweighted between country inequality in 2020, while at the same time, in an increase in population-weighted inequality. Ferreira et al. (2021) similarly show that the mortality burden of COVID-19, in terms of the life years lost to the pandemic, are positively correlated with GDP per capita, with richer countries bearing a larger share of mortality burden. At the same time, emerging evidence from advanced economies shows that within those countries, households with lower socio-economic status and those with more precarious jobs have been more affected, in terms of job and income losses, by the restrictions
# **4. Avenues for future research based on these data**

As mentioned, the primary purpose of this paper is to raise awareness of the COVID-19 trade policy data set and encourage its use. In this section we briefly sketch out possible research questions that are suggested by the patterns we observe in the data.

## **_4.1 Policy choice_**

A first set of research questions centers around understanding the motives underlying choices in the design and implementation of trade policy responses to the pandemic, reflected in the substantial crosscountry heterogeneity observed in the data. These include the timing, the duration, and the use of different instruments. Potential explanatory variables include mechanisms pertaining to the medical, the economic and the political spheres, e.g., public health parameters of the COVID-19 pandemic; features of the pre-crisis trade and trade policy structures, such as trade dependency, GVC participation and positioning; degree of existing protection; integration in multilateral or plurilateral trade policy initiatives; the political forces determining the quality of government action etc. An important corollary exercise would be to test whether and how such empirical relationships vary between the food and the medical sectors and potentially between more disaggregated product-level categories.

Herding effects could be considered as well, calling into question whether individual observed policy choice is independent of the choices of others. Another source of interdependence across policy choices arises from membership of regional trade agreements. In this regard, the role that the European Commission played in replacing and then reining back the export controls imposed initially by Member States of the European Union is worthy of further study.

Econometric analyses could be complemented by some well-chosen country case studies. For instance, the Indonesian government started by exhorting local producers not to sell masks abroad. Then, Jakarta imposed an export limit or share. When that did not ‘work’ they banned exports of masks. This sequence of policy steps is different than jumping in with an export ban in the first place, reflecting, potentially, different political economy factors.
We test this hypothesis by exploiting a sample expansion of the phone survey in Nigeria after the first 12 rounds of data collection.<sup>11</sup> Initially, the sample of households selected for the phone survey had constituted of a randomly selected subset of all households for which a phone number was available from the latest in-person LSMS-ISA survey: 4,934 households had a phone contact, 3,000 of whom were randomly selected and 1,950 were successfully interviewed in rounds 1-12 of the phone survey from April 2020 to April 2021 (1,050 were not interviewed due to nonresponse and failed contact). Starting from round 13 of data collection in November 2021, the remaining 1,934 households with an available phone number were contacted as well to expand the sample. This setup provides us with a (randomly selected) sample of respondents who had been previously interviewed and a (randomly selected) sample of respondents who were interviewed for the first time in round 13, and we can compare their reported vaccination status. We make the following prediction.

**Prediction 4:** Respondents interviewed for the first time, as opposed to repeat respondents, will display lower rates of vaccine uptake.

To test our prediction, we run the following OLS regression.

where _Di,s_ is a dummy variable denoting whether individual _i_ has been previously interviewed. In line with our prediction, we expect _β_ to be significant and positive.

# <u>Hypothesis 5: Proxy reporting biases</u>

When testing for respondent selection biases, one approach we explore is asking the purposively selected (main) respondent to report on the vaccination status of the remaining household members. However, such proxy reporting may be inaccurate (Davin et al. 2019; Li et al. 2015; Triplett 2010; Mosely and Wolinsky 1986). For errors in proxy reporting to drive the gap between survey estimates and administrative records, proxy reports would need to be systematically biased upwards, that is, main respondents would need
**Figure 1. World International Investment Positions: Bilateral vs. Country-Level Data**

<!-- Start of picture text --> Panel A. Bank Loans and Deposits Panel B. Portfolio Investment<br>40 60<br>35<br>50<br>30<br>40<br>25<br>20 30<br>15<br>20<br>10<br>10<br>5<br>0 0<br>Panel C. Foreign Direct Investment Panel D. International Reserves<br>60 14<br>50 12<br>10<br>40<br>8<br>30<br>6<br>20<br>4<br>10 2<br>0 0<br>Bilateral Country level (based on Lane and Milesi-Ferretti, 2018)<br>USD, trillions USD, trillions<br>2001 2002 2003 2004 2005 2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2001 2002 2003 2004 2005 2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018<br>USD, trillions USD, trillions<br>2001 2002 2003 2004 2005 2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2001 2002 2003 2004 2005 2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018<br><!-- End of picture text --> Note: This figure compares year-end values of world international investment positions for the bilateral data constructed in the paper and the country-level data constructed by Lane and Milesi-Ferretti (2018). Bilateral data are at the country-pair level and we obtain country-level data by aggregating values for each source country to all destination countries per year. For each year, we keep countries that appear in both samples and aggregate data across all countries. For comparison purposes, we include offshore financial centers (OFCs). For the rest of our analysis, we exclude these countries
assumptions, economic theory, formulae and empirical issues related to the model so that estimations can be replicated with the same methodology for different products and in different countries.

This first version of the tool-kit aims at being simple and focused. The focus is on selected data, products, assumptions, inputs, outputs. The intention is to provide answers for standard cases and data settings. The only data required is one cross-section household survey. Products are stylized into two prototypes described as singled priced goods (such as bread or sugar where prices are fixed irrespective of quantities consumed) and multiple priced goods (such as utilities where prices change according to quantities consumed). Assumptions are limited to the medium-term scenario where we consider inflation and behavioral changes but not savings and investments. The inputs of the model are the price change, inflation and elasticities and the outputs are changes in household welfare and government revenues.

The work <u>complements other efforts carried out by the World Bank on micro-simulations such as the</u> package ADePT and should eventually be integrated into ADePT in a second stage of the work. During the first stage of the work, we expanded on the treatment of inflation, elasticities and multiple priced goods. There is an explicit treatment of inflation as a separate effect from the price shock simulated. An effort is made to provide guidelines for the estimation of demand elasticities for different types of goods. For the first time, we distinguish between single priced and multiple priced goods and provide tools for the analysis of both types of goods. In particular, the case of multiple priced goods is treated in detail with the support of economic theory and estimation formulae for household welfare and government revenues.

4
# Financing Municipal Water and Sanitation Services in Nairobi’s Informal Settlements<sup>∗</sup>

## Aidan Coville

Sebastian Galiani Paul Gertler Susumu Yoshida

### _JEL Codes_ : C93, D04, O18

### _Keywords:_ Water and Sanitation, Informal settlements, Enforcement, Financial sustainability.

> ∗ _Affiliations_ : Coville: DIME, World Bank, acoville@worldbank.org; Galiani: University of Maryland and NBER, galiani@umd.edu; Gertler: UC Berkeley and NBER, gertler@berkeley.edu; Yoshida: DIME, World Bank, syoshida@worldbank.org.

_Human Subjects and Study Registration_ : The study received local and international ethical clearance from Maseno University (MSU/DRPC/00070/14) and Innovations for Poverty Action International Review Boards (Protocol : 13December-004). The study was registered in the American Economic Association RCT registry (AEARCTR-0003556) _Acknowledgements_ : The authors are grateful to the World Bank’s Strategic Impact Evaluation Fund (SIEF), Development Impact Evaluation Department (DIME), J-PAL/MIT Urban Services Initiative and the International Growth Center for financial support. The authors have benefited from comments by Edward Glaeser, Marco Gonzales, Kelsey Jack, Bryce Millett Steinberg, Guadalupe Bedoya, Gustavo Saltiel, Catherine Signe Tovey, Josses Mugabi, George Joseph, Ruth Kennedy-Walker, Jeffrey Mosenkis, Laura Burke, Douglas MacKay, Chris Prottas, Mitsunori Motohashi, Martin Gambrill, Arianna Legovini, Keziah Muthembwa, Camille Nuamah and participants in the 2019 Cities and Development conference, the 2020 NBER Summer Institute Urban Economics Conference, and from a seminar at NYU in Abu Dubai. The study would not have been possible without the continued efforts and long-term collaboration with the Nairobi City Water and Sewerage Company staff including Nahashon Muguna, Jackson Munuve, Kagiri Gicheha, Jason Mwangi, Beldina Owade, Christine Machio, Paul Mwarania, Ephantus Mugo, Martin Nangole, Lucy Njambi, Daisy Nyaboke and Owen Wanjala. Likewise, we thank Christine Ochieng, Paul Mbanga, Wendy Ayres, Rajesh Advani,
have moved up in the ranks. Points above the line are cities that dropped in the relative size distribution. The largest changes are among the middle and lower ranked agglomerations.

**Figure 5: Changes in population rank order between 1970-2000**

<!-- Start of picture text --> 140<br>120<br>100<br>80<br>60<br>40<br>20<br>0<br>0 20 40 60 80 100 120 140<br>Population rank 1970<br>Population rank 2000<br><!-- End of picture text --> Source: IPEA, IBGE

# **2.2. Patterns of Income Growth**

The second aspect of city performance that we investigate here relates to economic performance. We employ average household income as a proxy for productivity increases, since neither firm level factor productivity, nor data on real wage rates are consistently available for the time period 1970-2000. However, income and wages are strongly correlated in both levels and rates of growth for the years in which both are available at the município level (1991 & 2000). Annex 1 provides details.

As a second caveat, our data represent “nominal” incomes per capita, not “real” incomes. While the average agglomeration income figures have been adjusted for inflation over time, they do not reflect purchasing-power-parity [PPP] estimates across space—i.e., they do not consider local 12
go beyond the year 2000, from which the markup level started to decrease again with a sharp decline between 2001 and 2002.

Figures 2 and 3 showed that while average markup computed on materials declined over the decade, markup computed on labor increased except for small firms. This seems to suggest that firms hold different amounts of market power in the product and labor market. A trade-off hypothesis can therefore be formulated: firms that face higher competition compress wages to make up for lost margins on the product market. This hypothesis is the starting point for analyzing resource misallocation, which is commonly found in Africa and other developing regions (Restuccia and Rogerson, 2013).

# **5 Trade Openness and Market Power**

Three main research methodologies–structural models, randomized control trials, and quasi-experimental–methods have been used to study the welfare effects of trade policy (see Goldberg and Pavcnik (2016) for an overview and description of the methods). The article builds upon a quasi-experimental research design to detect the effect of trade policy on firms’ market power. The key challenges to address in the setup of the quasiexperimental design concern potential endogeneity, anticipation, and uncertainty of trade policy. The process trade liberalization in Ghana discussed in section 2.1 is referred to in seeking ways to overcome these difficulties in the identification strategy of the estimation methodology

## **5.1 Identification Strategy**

Using a difference-in-difference estimator in a quasi-experimental framework, it might seem natural to use the tariff rates in 1995 (the year of Ghana’s WTO accession) to estimate the _ex ante_ and _ex post_ impact of WTO accession on the outcome variable. However, such an approach does not adequately take into account the full trade liberalization process that took place in Ghana. First, tariff reductions started with conditionalities imposed by the SAP in 1991. Second, and perhaps most importantly, the breakthrough in the Uruguay round of negotiations was common knowledge; therefore, as Ghana had just begun to embark on trade liberalization under the IMF
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and 4 Asian countries for which comparable data are available. The 12 African countries include all those on Table 3 except Zimbabwe and Mozambique, for which it was not possible to break out employment in rural towns, and Ivory Coast where data from only one region was available. We have plotted nonfarm employment percentages rather than densities, because in cases such as these, where complete rural employment data are available, percentages are less susceptible than are densities to noise introduced through differences in working age classifications and measured female participation rates. The raw data come from the same sources reported in Table 3 adjusted to include rural towns up to 250,000 in size.

Figures 1 and 2 depict a positive relationship between rural nonfarm employment and both per capita GNP and agricultural income, thus supporting Hypotheses 3 and 4. Correlation coefficients for the African countries portrayed stand at .41 and .33, respectively. Extending the range of observation, the Asian data reinforce both of these conclusions. In addition, Figure 2 indicates that, for any given level of agricultural income, Asian countries generate higher levels of nonfarm employment than do their African counterparts, thus suggesting that agricultural multipliers may be higher in Asia.

Only in testing the effect of population density do the African cross-section data appear ambiguous. Except for Rwanda, the outlier in the lower right, the African data imply essentially no correlation between population density and rural nonfarm employment. Yet extrapolation to population density levels common in Asian countries does suggest a positive relationship. Perhaps 50-100 people per square kilometer represents a threshold level necessary for population density to play a discernible role in stimulating rural nonfarm activity. Lending credence to this notion, the Nigerian data in Figure 4 indicate a strong .87 correlation between population density and adult rural nonfarm employment (.78 for children) in
Housing<br>finance<br>access|Low|2.38|3.87||Performance|
|(proportion of population who<br>can access mortgage rate in SSA)|Lower middle<br>Upper middle|16.26<br>35.72|20.26<br>11.41|High|order is: UM, LM,<br>L.|
|Housing demand|Low|112.73|127.9||Performance|
|(annual housing demand)|Lower middle<br>Upper middle|115.33<br>23.67|201.33<br>34.58|Low|order is: UM, L,<br>LM.|
|Cheapest housing price (price of|Low|40388|58999||Performance|
|the cheapest, newly built house<br>by<br>a<br>formal<br>developer<br>or<br>contractor)|Lower middle<br>Upper middle|37381<br>32308|23090<br>22674|Low|order is: UM, LM,<br>L.|
|Housing input price<br>(cost of standard 50kg bag of|Low<br>Lower middle|12.21<br>10.42|5.1<br>1.96|Low|Performance<br>order is: UM, LM,|
|cement in US$)|Upper middle|7.61|0.53||L.|

_Source_ : Authors’ calculation based on a collection of data from a survey, the World Bank and Housing Finance in Africa yearbooks 2010, 2011 and 2013. Available at: www.housingfinanceafrica.org (accessed: 08/09/2014). _Notes_ : All measures are in US$. The countries included in each group are: (1) Lower income countries
This paper helps answer these questions through an evaluation of the impact of the Minas Fácil Expresso program in Minas Gerais, Brazil. This was a program designed to extend a business simplification program already present in the most populous municipalities in the state to its remaining municipalities. It was implemented first in 55 of the 822 unserved municipalities. We have 56 to 58 months of administrative data on firm registration rates and business tax receipts for each municipality, and show how difference-in-differences estimation can be used with such data to evaluate the impact of municipal reforms. Many of the non-treated municipalities are significantly smaller in population and had far fewer registrations pre-reform than the treated municipalities, which may make the differencein-differences assumption of common underlying trends less believable. We therefore use propensityscore matching and nearest neighbor matching to obtain a control group of more comparable enterprises, as well as using a group of municipalities in which the units were planned to be implemented but were not as yet implemented as an alternative control group.

Our preferred estimates show that municipalities opening a Minas Fácil Expresso office had a reduction of about 1.3 firms per month registering as a result of the reform, approximately a 10 percent reduction. This impact appears to be concentrated in the month of opening and month immediately after, with registration levels suffering less of a reduction in subsequent months. This result is robust to multiple different choices of a control group, to omitting one month with extraordinary registration patterns, and to the use of either difference-in-differences or fixed effects specifications. Consistent with no big changes in new registrations, we find municipalities do not receive any increase in businesses taxes as a result of the reform.

In addition to documenting the impact of this particular reform, we hope this paper can help serve two further related purposes. First, the administrative data used in the paper should be available for many other developing countries and the methods used here could thus be readily mimicked to evaluate other such municipal reforms. Such analysis is very cheap, and so we hope this paper might motivate other governments to