rafmacalaba/data-use-mentions-extended huggingface dataset:
sup><sup>_τ i_</sup> _t_<sup>indicatethatfalling</sup> trade costs are followed by an increase in the propensity to export as well as in the export value within industry-country-year bins. Interestingly, product standard harmonization seems to be more important than tariffs for the propensity to export. Henceforth, I make use of detail firm level data to show that the impact of harmonization on trade flows is due to the entry of new exporters —the extensive margin— rather than an increase in the export value of established exporters —the intensive margin.

An issue to be addressed is the possible endogeneity of my measure of product standards harmonization ( _NHt_<sup>_i_)duetoreversecausality:IfhigherU.S.exportvaluetotheEUtriggersharmo-</sup>

> 21Note that an increase in harmonization of standards —a reduction in an NTB to international trade— implies a reduction in _NHt_<sup>_i_.</sup>

> 22Helpman et al. (2008) estimate _Wjt i_<sup>asapredictedcomponentfromaprobitregressiononthepropensityto</sup> export. I compute it from the underlying firm level data. Details of the construction of the variables are in appendix 2.

> 23Austria, Belgium, Denmark, Finland, France, Germany, Greece, Ireland, Italy, Luxembourg, Netherlands, Portugal, Spain, Sweden, and United Kingdom.

> 24Year fixed effects control for observable and unobservable characteristics that change across years and are common to countries and industries; like exchange rates and other type of European trade policy tool. Industry fixed effects control for characteristics that vary across industries but not across years or across countries.

> 25The propensity to export is a dummy variable which is equal to one if there are positive export flows at the industry-country-year level.

> 26The lagged decision to export is represented by a dummy variable that is equal to one if there were U.S. exports in industry _i_ to country _j_ in the preceding period.

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third of the distribution did not grow at all. As a result, regional inequality increased, which is robust to the choice of inequality measure. This rise in regional inequality was driven by increasing inequality between countries, i.e. increasing dispersion in average living standards across countries. This contrasts with results at the global and East Asia level where within-country inequality increased.

The share of the regional population that is covered by a household survey that can be included in our database increased from 68% to 76% over this period. However, around a quarter of the population remains uncovered, and they are likely to live in some of the poorest countries in the region. Therefore, it is plausible that the estimates of inequality presented here are a lower bound on the true inequality. In addition, the latest available benchmark year is 2008, while GDP per capita has grown strongly since then. Thus it would be interesting to understand whether this growth at the macro level translated into gains in household consumption and what its distributional incidence was.<sup>53</sup> In order to move forward with this research agenda, we thus need more recent data and better coverage of the poorest countries, for which there is an emerging consensus among a number of actors (e.g. World Bank, 2015).

> 53 Between 2009 and 2014, regional real GDP in Sub-Saharan Africa grew at 5% on average (IMF, _World Economic Outlook_ 2015), compared with the average real growth of 4.8% during 1993 and 2008 (the period analyzed in this paper). In fact, during the latter period, Africa grew faster than other regions except Asia for which average real growth was about 6%. Furthermore, Sub-Saharan Africa avoided the slowdown experienced globally and in all regions except Asia. Nonetheless, it is important to note that population growth in Africa has been stronger than in other regions (about 2.4% per annum during 1993 and 2008, and 3% per annum during
child mortality—it will be possible to generate baseline data using the data from the 3-year survey, since such data are inherently retrospective.

The MV protocol does acknowledge “that the absence of pure baseline data from comparison villages is a limitation.” But this is insufficient treatment of a very important issue. The lack of broad baseline data on comparison villages is one more reason why differences between treated and comparison villages cannot be scientifically attributed to the intervention.

The protocol describes the problem and asserts that “[f]or many indicators, in the absence of new interventions it would be unlikely that substantive year on year changes would be witnessed, such as malaria prevalence, institutional delivery rates or child nutrition.” The implicit argument is that if we assume that little changes without interventions, data for the comparison villages from the three-year point can be interpreted as roughly equivalent to baseline data. The protocol also notes that the “presence of external interventions in comparison sites will be monitored throughout the evaluation to better understand the nature of secular changes taking place during the project period.” There are a number of problems with this argument. First, changes may occur for hard-toidentify reasons that have nothing to do with local interventions. Economic growth, weather variation, changes in remittance flows, broad improvements in public administration, and national information campaigns are examples of factors that could change conditions in the comparison villages but not be identified as “external interventions” by the MVP monitoring teams. Second, while changes over a single year for many indicators may typically be negligible for many indicators, over the relevant period of three years changes are more likely to be substantial. Third, if the MVP monitoring did find identify interventions, it would not be possible to credibly adjust for them in the evaluation. Instead, the existence of external interventions which may have changed conditions in the comparison villages would only make it clearer why it is essential to have baseline data at those sites.<sup>22</sup>

> 22 In describing the
finance from the introduction of credit bureaus affects job growth, then we should expect to see larger effects for firms in industries that are more dependent on external finance.

We use two complementary sources of firm level data: cross-country World Bank Enterprise Surveys that include information on 52,231 firms operating in 70 developing countries; and Bureau Van Dijk’s Orbis database on over 1 million firms operating across 29 developing countries. Both databases include large and small, and listed and unlisted firms. While the Enterprise Surveys provide data across a larger number of countries, the panel dimension in the Orbis database allows us to control for unobserved heterogeneity at the firm level, using firm fixed effects.

We find a strong positive relationship between access to finance and job growth. Overall, firms with access to a loan exhibit employment growth between 1 and 3 percentage points larger than firms with no access to finance across the two databases. These results are robust to controlling for firm fixed effects. When identifying the relationship using the introduction of credit bureaus (CB) as an exogenous shock to the supply of credit, we find that the introduction of CBs increases employment growth by over 5 percentage points compared to countries where CBs do not exist, a result that holds when estimated with the matched sample. This effect is particularly large for firms in industries that are more dependent on external finance.

We also find the association between finance and job growth to be stronger among MSMEs than among large firms. MSME firms with access to a loan have between a 1 and 4 percentage point larger employment growth than MSMEs without a loan across the two databases. This difference in job growth among MSMEs with and without access to finance is at least three times larger than the differential among large firms with and without a loan.<sup>7</sup> In our

> 7 We find similar results in robustness tests using alternative measures of access to finance such as growth of financing and debt ratio. A one standard deviation increase in the growth of financing among
22 economy story might suggest that NTMs are endogenously more prevalent in industries where trade is more important (i.e., trade volume is higher or has recently increased) if they are intended to protect domestic producers from foreign competition. In this case, empirical studies using industry panel data might understate the trade impact of NTMs (for an application see Ederington and Minier, 2003).<sup>12</sup> Thus, researchers must take into account that NTMs and trade flows are both endogenously determined in calculating the incidence and trade impact of NTMs.

Some of these problems are dealt with in the empirical studies discussed below. However, it is in general not possible to address all these issues at the same time. For this reason, any review of the landscape of non-tariff measures as well as the analysis of their impact on international trade is likely to be incomplete.

# **2.3 The trade impact of NTMs**

While governments impose non-tariff measures for a variety of reasons that may have nothing to do with international trade, NTMs may still have an impact on trade flows. The quantification of these effects is the subject of a large literature that is briefly reviewed below.<sup>13</sup> While frequency and coverage ratios are helpful in providing insight into the incidence of non-tariff measures (e.g., in which industries they are most common), they provide little guidance as to their trade restrictiveness. Thus, in the following subsection (2.3.1) we provide some general discussion of the main methodologies behind calculating the trade impact of NTMs. Obviously a significant issue in measuring the trade impact of NTMs is going to be _dimensionality_ : that NTMs can take many disparate forms that can have very different effects on trade flows. In light of this, one approach to measuring the trade impact of NTMs is to focus on a single type of NTM (e.g., TBT or SPS measures). The first subsection (2.
associated with the between-market move, which we will elaborate later on.

**Significance of job options.** There are multiple job options workers can compare from each labor market, and workers choose one job in every period. Which labor market a worker belongs to is not a direct choice, but rather an outcome of her choice of a job. If a worker chooses the job _j_ , then she belongs to the labor market _kj_ . This assumption is more realistic and introduces an important dimension through which aggregate shocks affect labor markets. The status of an economy impacts not only relative wages across markets but also the number of job options workers can choose from. The mass of tasks operated by producers responds to the shock, and the set of jobs expands (contracts) as the number of tasks increases (decreases). If the set of jobs expands, workers are able to sample more job options, and thus it becomes more likely to find a better job with a larger expected value. The sampled job options of our model are analogous to the vacancy concept in the search literature. When economic conditions improve, producers expand the task space by increasing _Tt_<sup>_k_.Then,the</sup> number of sampled job options increases, as workers are assumed to sample jobs at a constant rate. This relationship is determined at the general equilibrium which we will discuss after characterizing international trade. Our model brings the endogenous number of choices into an otherwise standard and easily tractable discrete choice model. Different from the search framework, the parameters of the model can be easily estimated using only labor market data, since the model provides simple equations that can be identified using only information on labor mobility.

Instead of choosing a job from job options available in each labor market, workers have an option to move to the residual labor market. Empirically, unemployment, home employment, and working in the informal sector all belong to this choice.<sup>20</sup> Each worker compares the
# **1 Introduction**

The last decades have seen a remarkable expansion in the number of subnational units across the world and their roles in providing public services (Gadenne and Singhal, 2014; Grossman and Lewis, 2014; Dahis and Szerman, 2023). As their role in service provision increased, so did their economic relevance – in Brazil, municipal procurement was equivalent to approximately 3% of GDP between 2002 and 2019, or about 25%-30% of total purchases by all levels of government – federal, state, and municipal (Thorstensen and Giesteira, 2021).

Data on local governments are often only available at an aggregate level, e.g. the total amount of purchases of goods and services, the total amount spent on health services, and the total amount of accrued liabilities. Consequently, many simple yet important questions related to the public finances of these units remain unanswered. Which are the suppliers of local governments, and what are their characteristics (e.g., size, location)? What is the share of purchases that happen through competitive tenders versus non-competitive methods? When competitive auctions take place, what is the degree of competition?

Another crucial dimension of local governments’ finances is how they execute their budgets. While aggregate commitment and spending amounts are easier to come by, we know little about the details of the budget execution. For instance, how long does it take to pay suppliers after deliveries are recognized? Is there a large variability in the payment timeliness across purchases within the same government? Do governments treat suppliers equally regarding payment timeliness? Answers to these questions can shed new light on the effectiveness of local governments and on their interaction with other economic agents. Similarly, when facing liquidity constraints, do governments prioritize the payment of some government functions at the expense of others? Payment delays impose several costs on suppliers and might affect the provision of public goods (Flynn and Pessoa, 2014). The importance of this issue is reflected in several recent regulations
in micro-data for emerging countries, a topic that has received very little attention in the literature.<sup>1</sup> We rely on high-quality matched employer-employee data from administrative records in Brazil and Uruguay, which allows us to obtain accurate measures of wages and to properly track worker mobility. The analysis is carried out using the maximum likelihood estimator first proposed by Altonji and Devereux (2000), and extended to consider DRWR by Goette et al. (2007). The estimator relies on a model of wage changes that jointly estimates the relevant parameters governing the process of DNWR and wage indexation. Importantly, the price index underlying the indexation process is endogenously determined by the model and allowed to be heterogeneous across workers. This permits ex-post evaluation of the relationship between this price index and different prices in the economy, which is crucial for understanding the sources of indexation. The model also allows for errors in the measurement of wages. This is potentially important, since measurement error in wage data has been shown to be a source of downward bias in studies of DNWR (Gottschalk, 2005).

Our results indicate that Brazil and Uruguay present substantial differences in the nature of wage rigidities, and in their reaction to changes in the macroeconomic and institutional environment. In the private formal sector of Uruguay, the pegging of individual nominal wage growth to the rate of inflation falls dramatically over the sample period. Downward real wage rigidity affects on average 75 percent of the workforce in the period 1996-1999, reducing to a fairly stable 7 percent for the rest of the sample period (1999-2004). In parallel, the fraction of workers subject to DNWR increases from around 13 percent in the first three years to an average of 66 percent in the second part of the sample. Hence, disinflation is associated with a sharp movement away from wage indexation. However, this process does not lead the way to a frictionless wage setting regime. Instead, worker resistance to nominal wage cuts arises.

In contrast with Uruguay, the incidence of wage
Although our study focuses on college students and white-collar workers in Bogot ́a, prejudice toward in Colombia and Latin America is even migrants pervasively widespread across individuals with varying levels of education, as observed using data from the public opinion survey Latinobarometro (Figure A.1). In fact, prejudice against migrants is positively and strongly correlated with the stock of the migrant population (Figure A.2). Therefore, this study is informative for policy-making in countries that host many migrants and want to reduce prejudice in the short term. Moreover, individuals with high levels of education could contribute donations and taxes as well as financially through offer political support to bolster vulnerable populations. Thus, they are worth studying.

We document two main findings. First, the interventions successfully improved prosociality and attitudes toward migrants. Participants assigned to either the game or the video were approximately 11 percentage points (pp) more likely to donate to the charity that supports Venezuelan migrants than participants assigned to the control group, equivalent to a 16 percent increase. The game itself improved self-reported trust towards Venezuelans by 0.29 standard deviations (sd) relative to the control group. Regarding attitudes towards migrants, both treatments had a positive and significant impact on the assessment that migrant poverty was due to circumstances beyond a migrant’s control, rather than to a lack of effort on their part. Moreover, both treatments had positive and significant effects on policy attitudes about government assistance to migrants.

We also find that, per minute spent on each intervention, the video was at least four times more effective than the game in improving prosocial behaviors and attitudes toward forced migrants. This conclusion holds weight, especially considering the game’s demand for greater attention and active engagement, along with its limitation to a specific platform. The video’s shorter duration and seamless scalability across online platforms make it a more favorable choice for fostering prosocial behaviors in the short term.

In addition, we evaluated if the treatments affected the empathetic concern and perspective5
of output, as domestic consumption and investment. ICIO tables, which have been developed combining national IO statistics with trade data, describe sale-purchase relationships between industries within and between economies as well as the uses in different final demand components (e.g. consumption, investment and government spending). In particular, an ICIO table specifies the country-sector pairs that provide intermediate inputs to a given industry and the country-sector pairs to which that industry sells its output - in the case of intermediate products - or the ultimate destination markets for final goods. In Appendix A we present the basic conceptual framework of ICIO models while in Section 2.1 we show how to load ICIO tables with the command `icio_load` .

# **2.1 Implementation: Loading ICIO tables using the** `icio_load` **command**

In order to use the `icio` command one needs to load a particular ICIO table by using the `icio_load` command. `icio_load` allows to work directly with the most popular ICIO tables - OECD TiVA database (OECD, 2018), World Input-Output Database (WIOD, Timmer et al. 2015), and Eora Global Supply Chain Database (Lenzen et al. 2013); in addition, any other user-provided ICIO table can be loaded.

## **2.1.1 Syntax**

The basic syntax for `icio_load` is

- `icio_load, [` _options_ `]`

where the main _options_ are:

- <u>`iciotable(`</u> _table_ _~~n~~ ame_ `[,` _usertable_ _~~o~~ ptions_ `])` , specifies the ICIO table to be used for the analysis; _default_ is `wiodn` , the last WIOD release available (release 2016, see below for more details on the available tables’ versions);

- <u>`year(`</u> _#_ `)` , sets the year to be used for the analysis
and Nicoletti, C. (2006), ‘Intergenerational mobility and sample selection in short panels’, _Journal of Applied Econometrics_ **21** (8), 1265–1293.

- Girdwood, S. and Leibbrandt, M. (2009), ‘Intergenerational Mobility: Analysis of the NIDS Wave 1 Dataset’, _National Income Dynamics Study Discussion Paper_ **15** .

- Glewwe, P. (2005), ‘How Much of Observed Economic Mobility Is Measurement Error? A Method to Remove Measurement Error, with an Application to Vietnam’, _Unpublished paper, World Bank, Washington, DC_ .

- Grusky, D. B. and DiPrete, T. A. (1990), ‘Recent trends in the process of stratification’, _Demography_ **27** (4), 617–637.

- Hackman, E., Emanuel, I., Van Belle, G. and Daling, J. (1983), ‘Maternal birth weight and subsequent pregnancy outcome’, _Jama_ **250** (15), 2016–2019.

- Haveman, R. and Wolfe, B. (1995), ‘The determinants of children’s attainments: A review of methods and findings’, _Journal of Economic Literature_ **33** , 1829–1878.

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**2017-18**|**2018-19**|**2019-20**|
|---|---|---|---|
|Treatment|902|710|468|
|Control|412|296|330|

Both control and treatment schools experienced changes in PqTR, repetition rate, and dropout rate year-on-year. To capture the differential dynamics between treated and control schools, we employ difference-in-difference (DiD) analysis.

**Table 5.2** (in Section 8, Tables) presents DiD estimates for the impact of treatment on PqTRs. As expected given the definitions of treatment and control, treated schools experienced decline in PqTR compared to control schools in each year – an substantial decline of 41 pupils per qualified teacher.

**Lagged effects for dropout and repetition.** Because dropout and repetition rates are determined by schools at the end of a school year, there is an expected ‘lag’ in impacts for an improvement in school staffing. Recall that new teachers are typically deployed to schools at the start of the new school year in September, with the EMIS data collection taking place around two months later in OctoberNovember. In order to allow time for the impacts of new teachers to be felt and measured, we report lagged effects for these indicators from the following year’s EMIS data. For example, to evaluate the impact of teachers allocated in August/September 2017, we compare:

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