rafmacalaba/datause-encoder-data huggingface dataset:
shipment being the true transactions price are the same for administering SSG actions as for administering ordinary customs duties. The formula for calculating the additional duty that may be applied to any shipment is more complex than that for the volume trigger, but could be programmed by a competent technician in a short time.

The major administrative constraint on applying such measures (volume or pricebased) is the requirement that the products on which measures might be applied had to be so marked when the post Uruguay-Round schedules of agricultural tariffs were submitted.

The SSG’s price trigger system allows the importing country government to screen each shipment against trigger prices, but once the trigger prices are posted, a system such as this will be in large part self-enforced by exporters. Unless exporters raise their prices to the level demanded by the additional duty formula, that difference will be added by the importing country’s authorities – the buyer will pay the higher price, the choice the exporter faces is to collect the higher price himself or see the importing country government collect it.

It was therefore no surprise that immediately the Uruguay Round agreements went into effect, several Members notified ‘up-front’ trigger prices for the tariff lines on which they had reserved the right to apply SSG measures.<sup>60</sup> The EEC and the US, for example, notified complete schedules of trigger prices in 1995. Korea notified trigger prices for 12 tariff lines in early 1995; notified the remainder its schedule in September 1996. Canada posts up-front volume as well as price triggers, the volume triggers are recalculated each year.<sup>61</sup>

# <u>Notification requirements</u>

As to notification of SSG actions, WTO Members have agreed standardized formats for how they will report.<sup>62</sup> The document prescribes an ‘Annual summary of special safeguard actions taken,’ in the format of ‘Table MA.5.’ The following, taken from Japan’s notification of actions in 1995, illustrates format and content.<sup>63</sup> 60 The AoA (Article 7) requires that any Member applying a volume triggered SSG measure must notify the WTO ‘as far in advance as may be practicable and any event within ten days of the implementation of such action.’ Canada’s (discussed elsewhere in this annex) is the only example of up front notification of volume triggers.

61 The EEC notification is reported in WTO document G/AG/N/EEC/2 (8 August 1995), United States trigger prices in G/AG/N/USA/1 (10 February 1995); Korea in G/AG/N/KOR/2 (1 June 1995) and G/AG/N/KOR/6 (12 September 1996). Canada’ price and volume triggers are available at Agriculture and Agri-food Canada, ‘Notice of Special Agricultural Safeguard Price and Volume Triggers,’ at http://www.agr.gc.ca/itpd-dpci/technical/ssg_e.htm.

62 WTO document G/AG/2 (30 June 1995) Committee on Agriculture, Notification Requirements and Formats.

63 Taken from WTO document G/AG/N/JPN/7 (8 May 1996) 45
# _Note on attrition weight construction_

We calculated inverse probability weights (IPW) separately for the four groups used in the panel cohort analyses, i.e., children under or over three years old in migrant or non-migrant households, using an approach similar to Molina Millán and Macours (2017). First, we constructed approximately 40 indicators based on the 2008 survey. In addition to the variables in Tables 1a, 1b, 4 and Appendix Table 1, these included further measures of household characteristics (electricity, dirt floor, block walls, metal roof and home ownership), whether household members were in religious or other (e.g., sports) community groups, and measures that could facilitate recontact, including whether the household address, phone number or a neighbor’s name/address had been fully completed. <u>Second, we ran bivariate</u> regressions on an indicator of being interviewed in 2012 for each variable (separately for each age cohortmigration status sample). We retained for potential inclusion in the weight construction all variables significant at 10% in any model. Third, we estimated the probability of re-interview in 2012 with this set of baseline predictors for each age cohort-migration sample to calculate separate weights for each group. To account for collinearity between predictors, the baseline predictor set was further limited by conducting stepwise selection of variables with backward elimination and using the adjusted R<sup>2</sup> as the information criteria.

Controls for a quadratic of age, municipality fixed effects and an indicator for male child were fixed in the regressions. At each step, the iterative procedure removes from the model the predictor that most improves the information criterion until there is no variable whose removal improves it. We implemented this using ‘vselect’ in Stata (Lindsey and Sheather 2010). Fourth, using the final model for each subsample, we predicted for each observation the probability of having been re-interviewed and constructed the IPW. Sample weights ranged from 0.78 to 5.56 (25<sup>th</sup> percentile 1.10, 50<sup>th</sup> 1.21, 75<sup>th</sup> 1.36).

# **References:**

Lindsey, C. and S. Sheather. (2010). “Variable selection in linear regression.” _The Stata Journal_ , 10(4): 650–669.

Molina Millán, T. and K. Macours. 2017. “Attrition in Randomized Control Trials: Using Tracking Information to Correct Bias.” _<u>CEPR Discussion Paper No. DP11962</u>_
aggregation which measures what percentage of the 26 practices a business implements. We examine first the correlation between business practices and firm outcomes – sales, profits and productivity – in the cross section. The exercise is very much in the spirit of Bloom and Van Reenen (2007), and our results for the sample of microenterprises are remarkably similar to those in Bloom et al (2012): a one standard deviation improvement in business practices is associated with a 35 percent increase in labor productivity and a 22 percent increase in total factor productivity. The comparable relationships for much larger firms based on data from Bloom et al (2012) are 43 and 17 percent, respectively.

The cross-sectional analysis provides correlations without providing any evidence on the direct of causation. We then take two steps in the direction of uncovering causality. First, we provide some evidence using panel data available from three countries – Kenya, Nigeria and Sri Lanka. Using these data, we show that business practices measured at baseline are associated with higher rates of enterprise survival and higher rates of sales growth in the following year or years. Second, we assess evidence from the literature measuring the impact of microenterprise training programs. Overall, the evidence from entrepreneurship training programs disappointingly finds little evidence that training induces faster rates of growth (McKenzie and Woodruff 2012).<sup>2</sup> Focusing on five studies which measure business practices with a version of our instrument, we show that the effects on sales and profits found in these studies are always consistent with the predicted effects given the observed changes in business practices. Most of the studies find small, and statistically insignificant, effects on sales and profits because they find small effects of the training programs on business practices. Thus, we cannot conclude from the literature that business practices do not matter. The correct conclusion is that most of the existing training programs have effects which are too weak to generate statistically significant effects on outcomes.

In interpreting the data, we should keep in mind two ways in which the situation of small firms differs from that of larger firms. First, all of our data on both practices and outcomes are selfreported. We might be concerned that individuals who are prone to overstatement will overstate both practices and outcomes. We address this head on by conducting auditing exercises in two of the samples. We find that assessments of auditors hired by us, and blind to the survey responses

> 2 Calderon, Cunha and De Giorgi (2013) and Anderson-MacDonald et al. (2014) are recent exceptions, each showing more substantial growth following microenterprise training.

3
Figure A.10: The Impact of Reductions in Commission Fees and Tax Withholding Rates On The Use of Electronic Payment Technology

# A. Number of Card Transactions

<!-- Start of picture text --> 2009m1 2010m7 2012m1 2013m7<br>Year-Month<br>16<br>15.5<br>Log Number of Card Transactions<br>15<br><!-- End of picture text -->

# B. Volume of Card Transactions

<!-- Start of picture text --> 2009m1 2010m7 2012m1 2013m7<br>Year-Month<br>C. Number of POS<br>2009m1 2010m7 2012m1 2013m7<br>Year-Month<br>23.5<br>23<br>22.5<br>22<br>Log Volume of Card Transactions<br>21.5<br>11.4<br>11.2<br>11<br>Log Number of POS<br>10.8<br>10.6<br><!-- End of picture text --> Notes: These graphs are similar to those in Figure 1, Panel A, displaying time series aggregates, as per the panel titles. The vertical line marks January 2012, when withholding rates applied by credit/debit card companies were reduced (see Figure A.7) and commissions charged by credit/debit card companies were lowered (see Section 3.3). This figure is discussed in Section 6.

44
El Sakka and McNabb (1999) find that remittances to Egypt increase with country’s inflation. In a panel specification including 113 countries and up to 29 years, Chami et al. (2005) obtain that remittances to GDP are negatively correlated with the GDP growth.

Examining the determinants of remittances using a panel of 101 countries during 1970-2003, IMF (2005) finds a significant negative impact of home country output on remittances. Nevertheless, the study’s analysis of the correlations between aggregate remittances and other inflows on the one hand, and GDP on the other indicates that remittances are positively correlated with GDP, although they are not as sharply procyclical as the non-FDI capital inflows.

Acosta et al (2008) examine the correlation between the cyclical components of remittances and real output in recipient countries for 26 Latin American countries and find evidence of countercyclicality even after controlling for the endogeneity of output fluctuations. Extension of the analysis to other developing countries leads to the same result, but also reveals great heterogeneity by country group in the sensitivity of remittances to oscillations in the real output. The aggregated de-trended remittances sent to the 12 countries examined in Sayan (2006) are also negatively correlated with de-trended GDP. Nevertheless, both Acosta et al (2008) and Sayan (2006) find that the correlations at country-specific level weaken the verdict of counter-cyclicality obtained from the aggregate level analyses. Thus, several countries in the samples of each study exhibit pro- rather than counter-cyclical remittances in relation to output. This result prompts Sayan (2006) to conclude that “counter-cyclicality is hard to generalize to all countries.” Representing the literature which gives preference to the “portfolio” approach in remitting, Lueth and Ruiz-Arranz (2006) conclude that remittances are aligned with the business cycle in the recipient country. Their analysis is based on estimating a gravity model of the determinants of remittances in 11 countries. Lueth and Ruiz-Arranz (2007) employ time series data and a vector error correction model to find that remittances to Sri Lanka are pro-cyclical. In addition, the study compares remittances with other external flows and obtains a negative correlation between ODA and GDP, as well as positive correlations between remittances (private capital flows) and GDP. Finally, Giuliano and Ruiz-Arranz (2005) show that remittances are more pro-cyclical in countries with shallower financial systems.

6
# Pollution and Labor Productivity: Evidence from Chilean Cities

Charl Jooste<sup>1</sup> , Ted Loch-Temzelides<sup>1,2</sup> , James Sampi<sup>1</sup> , and Hasan Dudu<sup>1</sup>

> 1World Bank

> 2Rice University

## **JEL classification** : E24; Q52; Q53

**Keywords** : Labor productivity; Pollution; Developing economies

> *We thank the multi-donor Climate Support Facility for funding this project. We thank Paulina Schulz Antipa, Juan Jose Miranda, Ivailo Izvorski, Benigna Leiss and Erik von Uexkull for helpful comments and suggestions. All views expressed and remaining errors are those of the authors and not the World Bank or the Climate Support Facility.
- Cummings, C., J. Pacitto, D. Lauro, and M. Foresti (2015). _Why people move: Understanding the drivers and trends of migration to Europe._ Overseas Development Institute, London.

- Deiana, C., V. Maheshri, and G. Mastrobuoni (2024). Unintended consequences of search and rescue operations. _American Economic Journal: Economic Policy, forthcoming_ .

- Deiana, C., G. Mazzarella, E. C. Meroni, and L. Tiozzo Pezzoli (2023). The unexpected influencer: Pope Francis and European perceptions of the recent refugee crisis. _Oxford Economic Papers 75_ (1), 75–95.

- Del Prete, D., M. Di Maio, and A. Rahman (2023). Firms amid conflict: Performance, production inputs, and market competition. _Journal of Development Economics 154_ (103143).

- Di Maio, M., F. Fasani, V. Leone Sciabolazza, and V. Molini (2023). Facing displacement and a global pandemic: Evidence from a fragile state. _Journal of Demographic Economics_ , 1–26.

- Di Maio, M., V. Leone Sciabolazza, and V. Molini (2023). Migration in Libya: A spatial network analysis. _World Development 163_ , 106139.

- Djaji ́c, S. (2017). Transit migration. _Review of International Economics 25_ (5), 1017–1045.

- Djourelova, M. (2023). Persuasion through slanted language: Evidence from the media coverage of immigration. _American Economic Review 113_ , 800–835.

- Farr ́e, L. and F. Fasani (2013). Media exposure and internal migration—Evidence from Indonesia. _Journal of Development Economics 102_ , 48–61.

- Fitzgerald, M. and M. Toaldo (2016). A quick guide to libya’s main players. _European Council on Foreign Relations_ .

- Friebel, G.and Manchin, M., M. Mendola, and G. Prarolo (2023). International migration intentions and illegal costs: Evidence using africa-to-europe smuggling routes. _Journal of International Economica forthcoming_ .

- Giulietti, C., J. Wahba, and Y. Zenou (2018). Strong versus weak ties in migration. _European Economic Review 104_ , 111–137.

- Grubanov-Boskovic, S., S. Kalantaryan, S. Migali, and M. Scipioni (2021). The impact of the internet on migration aspirations and intentions. _Migration Studies 9_ (4), 1807–1822.

- IOM (2015). _Migration Trends Across the Mediterranean: Connecting the Dots_ . International Organization for Migration, Geneva.

- IOM (2016). _Displacement Tracking Matrix, DTM Round 1_ . International Organization for Migration, Geneva.

- IOM (2018a). _Displacement Tracking Matrix (DTM). Libya’s Migrant Report (Round 18). March, 2018_ . International Organization for Migration, Geneva.

21
Unfortunately for empirical work, K is unobserved. Even data on known mining reserves is inadequate as endogenous investments in exploration lead to new discoveries. As discussed, some studies use output of oil or mining as a share of GDP (e.g., Nunn 2008, Sala-i-Martin et al. 2004), which appear positively correlated with GDP per capita or subsequent economic growth. Other studies use gross export receipts as a share of total merchandise exports or as a share of GDP (e.g., Sachs and Warner 1997, 2001; BravoOrtega and De Gregorio 2007, Gylfason 2004). These proxies of natural resource dependence are found to be positively correlated with GDP per capita (Bravo-Ortega and De Gregorio 2007) but are often found to be negatively correlated with subsequent growth.<sup>11</sup>

# **V. Empirical Strategy**

The discussion above suggests that empirically the resource curse, like Dracula, is hard to nail down. More specifically, getting the right proxy for resource abundance, and understanding its properties, is critical to establishing the credibility of any empirical finding. The mining reserve measures are closest to measuring true abundance, but capture only a narrow range of products and hence do not obviate the need for a trade based proxy.

In taking up the search for the curse again, we follow the vast literature on growth empirics but with a couple of innovations that help us identify a floor of the effect natural resource endowments. A key innovation is the inclusion of the trade-data indicator of relative endowments, which has the desirable property of an expected positive correlation between natural-resource endowments per worker, which is not the case for the preferred proxies used by resource-curse believers. We also choose an institutional variable that is commonplace in the institutions and growth literature concerning the powers of the executive branch of government, which has been absent in the voracity effects empirical literature.

# _V. A. Empirical strategy: static and dynamic growth models_

If relative endowments were observed, an empirical income function consistent with the economic growth literature can be written as: (9) yi = a + h(ln(K/L)i) + f’Xi + ei , where the subscripts represent countries, a is the intercept, y is the natural logarithm of GDP per capita adjusted for purchasing power parity, X is matrix of other determinants of cross-country income differences, and e is assumed to be white noise error. The corresponding literature includes Frankel and Romer (1999), Acemoglu, Johnson and

> 11 Isham et al. (2005) used dummy variables to identify countries according to export structures by looking only at the top two merchandise exports (according to the three-digit SITC trade classification), which further confounds the notion of natural resource dependence. It is also noteworthy, as mentioned earlier in this paper, that papers that have relied on the Sachs and Warner data are actually using a observations that use the gross exports of natural resources as a share of merchandise exports where a couple of observations, Singapore and Trinidad & Tobago, were actually net exports of natural resources.

9
Once an applicant is selected in the random ballot, they must provide a valid job offer in New Zealand (unskilled jobs suffice) within six months in order to have their application to immigrate approved. These job offers are increasingly arranged by large employers visiting Samoa after the annual ballot results are announced. Once a job offer is filed along with a residence application, it typically takes three to nine months for an applicant to receive a decision and they are then given up to one year to move. If they are successful, their immediate family (spouse and dependent children up to age 24) can also move to New Zealand with them. This rule specifying which family members can and cannot accompany the successful migrant, coupled with the random selection amongst Samoan Quota applicants, is key to being able to overcome the selectivity issues raised in the previous section.

Conceptually, we can estimate the impact of migration on family members left behind by comparing outcomes for the group of households in Samoa that sent SQ emigrants to those for the group with unsuccessful ballots who would not be eligible to move their entire household to New Zealand had their Principal Applicant been chosen in the ballot. We next discuss the data that has been collected to allow us to implement this estimation approach.

# **3.3 The Samoa Labour Mobility Survey**

The data used in this paper are from the Samoa Labour Mobility Survey (SLMS) which was designed by the authors and implemented by the Samoa Bureau of Statistics in late 2008. The survey is based on a self-weighting sample of 622 households in 90 villages, drawn from all regions of Samoa. Out of these surveyed households, 78 had current or former members that were successful applicants to the Samoan Quota in the previous five years.<sup>6</sup> A further 121 households contained individuals that had applied at least once to the Samoan Quota in the previous five years and had never been successful. The remaining 423 households in the sample did not report having either former members who were now SQ emigrants or having current members who had applied to the SQ in the previous five years and are not used in this paper.

The SLMS measures both incomes and expenditures of the responding households. Five income components are considered: labor earnings, net (i.e., also taking account of outbound) remittances of both money and goods over the previous six months, net returns from sales of

> 6 We decided to focus on migration from the 2003-2008 ballots to limit issues in regards to the accuracy of recalling past experiences and because we also have access to limited administrative data on SQ migrants from these ballots.

11
marginal effect of 1.1 percentage points. We also estimated a random effects model on the full set of observations (118 countries). The results are similar to those obtained when including country fixed effects<sup>12</sup> and are reported in Appendix 3.

# **Violent uprisings**

Can a decrease in subjective well-being also explain violent resistance? We test whether this is the case using three different measures of violent political resistance, showing the results of the regressions in Table 5 (Columns 2-4). In Column 2, the dependent variable is the number of riots obtained from the CNTS data set. Riots are only included if they involve a clash of more than 100 citizens who use physical force. We transform the number of riots using the inverse hyperbolic sine transformation and estimate an OLS model with country and year fixed effects. In this regression, _suffering_ has a significant effect on riots, but the coefficient is only significant at the 10% level and is considerably smaller than when the dependent variable is nonviolent resistance. Whereas a percentage point increase in suffering increases nonviolent resistance by 2.1%, it only increases the number of riots by 1.3%.

To measure armed violent conflict, we use a dummy variable which is one if there is “a contested incompatibility that concerns government and/or territory where the use of armed force between two parties, of which at least one is the government of a state, results in at least 25 battle-related deaths in one calendar year” (Pettersson & Wallensteen, 2015, p. 1). We also measure the intensity of violent political conflict with the number of battle-related deaths. This variable is left censured at 25 battle-related deaths, as deaths are only recorded for recognized violent conflicts. We transform the number of battle-related deaths using the inverse hyperbolic sine transformation. Data for both violent conflict variables are derived from UCDP/PRIO (see Pettersson & Wallensteen, 2015).

> 12 A Hausman test does not find evidence of systematic differences between the fixed effects and random effects model and hence the random effects model is statistically most appropriate. For reasons discussed in our methodology section, we still have more confidence in the results obtained in the more conservative fixed effects model.

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