rafmacalaba/datause-encoder-data huggingface dataset:
suggests that there is space for Romania to increase its trade integration which can largely benefit productivity convergence. The same seems to happen to the other selected sectors.

**Figure 6 - Increase in average annual productivity Figure 7- Average openness to trade by sector: 2003-08 growth** **_by sector_ given a one standard deviation period augment of sectoral openness to trade over 2003-08**

<!-- Start of picture text --> period<br>40.0 18.0 17.1<br>15.9<br>33.7 16.0<br>35.0<br>14.0<br>30.0<br>12.0<br>25.0 9.9<br>10.0<br>20.0<br>8.0<br>15.0<br>6.0<br>10.0 7.7 6.2 4.0<br>5.0 2.0<br>0.0 0.0<br>Manufacture of basic Manufacture of motor Mining of coal and Manufacture of basic Manufacture of motor Mining of coal and<br>metals vehicles, trailers and lignite; extraction of metals vehicles, trailers and lignite; extraction of peat<br>semi‐trailers peat semi‐trailers<br>All countries Romania<br>percent<br>percent per year<br><!-- End of picture text --> Note: _one standard deviation of trade openness for the manufacture of basic metals, manufacture of motor vehicles, trailers and semi-trailers, and mining of coal and lignite (63.7, 15.5 and 42.8, respectively) are computed over the whole sample of countries for the 2003-08 period._

# **4. CONCLUDING REMARKS**

This paper attempts to shed light on the effect of trade and regulation on productivity convergence while focusing on the specific case of Romania. A model of labor productivity based on Conway et al. (2006) was adapted and estimated, first, at country the level over the 1995-2010 period for a set of 30 countries: EU countries, including Romania, plus Iceland, Norway and Switzerland. Proxying the regulatory environment by the regulatory quality indicator from the WGI dataset, the **country level** model has provided results which can be summarized as follows:

- Openness to global trade (measured both in relation to global trade as well as to trade with EU partners) is shown to have a positive impact on productivity convergence when controlling for the level of regulatory quality. The potential gains for increasing trade intensity in Romania are particularly high: a 10% increase in openness to global trade over the 1995-2010 period would have boosted productivity growth by 9.7 percent per year. A 10% increase in openness to EU trade, in particular, would have led to an annual increase in productivity of 7%.

- As the realization of the benefits from trade integration depends to some extent on regulation, the effects of regulation on productivity growth are shown to be positive, regardless of the indicator used to measure regulation, and both through direct and indirect channels. Simulation results also show how countries with different levels of regulatory quality would benefit from a regulatory improvement: had Romania improved its regulatory environment to the same level as Denmark in 2010, its annual productivity growth would have been 14 percent higher over the 1995-2010 period.

17
# **Appendix E: Robustness Tests**

||_(1)_|_(2)_|_(3)_|_(4)_|_(5)_|_(6)_|
|---|---|---|---|---|---|---|
|Ln bottom 40|−0.193***|−0.115*|−0.145**|−0.175***|−0.185**|−0.174**|
||(0.065)|(0.061)|(0.057)|(0.060)|(0.075)|(0.078)|
|Ln population|0.672***|0.489***|0.578***|1.108***|0.738***|0.691***|
||(0.120)|(0.083)|(0.084)|(0.095)|(0.118)|(0.103)|
|Capital|0.255*|0.436***|0.362***|0.505***|−0.047|0.384**|
||(0.151)|(0.140)|(0.130)|(0.155)|(0.133)|(0.163)|
|Observations|1,081|1,059|979|1,081|1,081|1,081|

_Note:_ Country fixed effects are included in all estimations. Standard errors clustered at the country level are shown in parentheses.

***p < .01 **p < .05 *p < .1

20
The second set of insights pertain to randomization inference. Since the marketlevel randomization in our study involves 18 randomizable units, asymptotic inference is unsuitable, so we use randomization inference. It is known that any scalar function of treatment and comparison groups is a statistic upon which a (correctlysized) randomization-inference-based test of the sharp null hypothesis could be built, but also that such statistics may vary in their statistical power in the face of any particular alternative hypothesis (Imbens and Rubin, 2015). We anticipated that, even with correctly-sized tests, the market-level portion of our design may present relatively low statistical power. Consequently, we conducted blinded analysis to choose, on the basis of statistical power, among testing approaches for several hypotheses: Hypothesis I, and a common framework for Hypotheses IV and V.<sup>16</sup> Hypothesis I is the test of whether applicants to different contracts vary in their TTC scores. Blinded analysis, in which we simulated additive treatment effects and calculated the statistical power under different approaches, suggested that ordinary least squares regression (OLS) would yield lower statistical power than would a Kolmogorov-Smirnov (KS) test of the equality of two distributions. Over a range of simulations, the KS test had between one and four times the power of OLS. We therefore committed to KS (over OLS and two other alternatives) as our primary test of this hypothesis. This prediction is borne out in Appendix Table C.1.<sup>17</sup> Hypotheses IV and V relate to the effects of advertised and experienced contracts on student test scores. Here, with the re-randomization taking place at the school level, we had many possible specifications to choose from. We examined 14 specifications (modeling random effects or fixed effects at different levels), and committed to one with the highest power. Simulations suggested that this could produce a 20 to 25 percent narrower confidence interval than in a simple benchmark specification. Comparing Table 3 to Appendix Table A.4, this was substantively borne out.<sup>18</sup> On the basis of this theory and analysis of blinded data, we settled on six primary tests: an outcome, a sample, a specification and associated test statistic, and an the data-blinding process. Results of the blinded analysis (for which IPA certified that we used only blinded data) are in our pre-analysis plan. Our RCT registry entry (AEARCTR-0002565) is accompanied by IPA’s letter specifying the date after which treatment was unblinded.

> 16Hypotheses II and III employ data that our team collected, so did not have power concerns associated with them; Hypothesis VI offered fewer degrees of freedom.

> 17The confidence interval for the KS test is roughly half the width of the corresponding OLS confidence interval: a gain in precision commensurate with more than tripling the sample size.

18Our pre-committed random effects model yields a confidence interval 86 percent as wide as that from OLS, commensurate with the power gain from increasing the sample size by a third.

13
may thus decide to either stay unemployed or accept jobs in the informal sector, which tends to initially offer higher hourly wages and other benefits such as lower costs of commuting to work.Job seekers may also decide to pursue formal sector work with temporary contracts, which offer starting wages that are slightly higher, but provide less job stability and fewer to workers.

The job search framework posits that a formal sector wage incentive lowers job seekers’ reservation wages and increases job search for formal employment. The exact magnitude of the respective change in effort and reservation wages depends on the job finding function ( _λf_ ( _ei,f,t|hi,t_ )). However, we can use the insight by Card and Hyslop (2005) that if job seekers do not change search effort - for which we find supportive evidence in our data<sup>26</sup> - the reduction of reservation wages is equal to the size of the incentive. This gives us a conservative upper bound for the drop in reservation wages to empirically test for the importance of wage expectations.

We find that reservation wages play an important role for employment choices. Figure 6 shows how treatment effects on the extensive (Panel A) and intensive (Panel B) margin differ when we divide our sample by participants’ baseline reservation wages. The group of youths with reservation wage under 3,000 pesos shows no aggregate treatment effect nor a switching between jobs with temporary and permanent contracts. For the second group with reservation wages between 3,000 and the average starting salary of 5,500 pesos we also do not find an aggregate effect on the extensive or intensive margin. However, there is an increase of 6 p.p. in the share with a permanent contract. The third group includes participants with reservation wages of up to 20% above the average starting salary level; this group should be most affected by the incentive if reservation wages are binding. We indeed find a large aggregate employment effect for this group. The share with formal employment increases by 15 p.p. (Panel A) and the aggregate time formally employed goes up by more than 3 months (Panel B). This sharp increase is exclusively driven by an increase in work with permanent contracts, while the share with temporary work and informal work slightly decreases (Panel A). Strikingly, the intensive margin increase in (permanent) formal employment comes almost entirely from a reduction in informal work (Panel B), illustrating the importance of reservation wages for youths’ career choices. By contrast, we do not ob-

> 26Specifically, we find that in the endline survey that the treatment group does not report higher level of job search activities. One limitation of this evidence is that we only collect job search data for the endogenously determined subgroup of people without work in our sample.

29
between the second quarter of 2008 and the first quarter of 2009. Since intra-GPN trade is especially sensitive to changes in the trade costs (Section 5; Yi, 2003), this can explain the magnified fall in trade compared to GDP.

A final explanation that has received less attention is the role of bullwhip effects in global supply chains on the trade collapse (Escaith and Gonguet, 2009; Escaith, Lindenberg and Miroudot, 2010; Ma and Van Assche, 2010). The bullwhip effect is one of the most researched and documented symptoms in the field of supply chains management (Lee, Padmanabhan and Wang, 1997; Cachon, Randall and Schmidt, 2007). It states that, when a downstream firm is confronted with a drop in demand for its final products, its first reaction is to run down its inventories. Thus a slowdown in downstream activities transforms itself into an amplified reduction in the demand for inputs that are located upstream.<sup>20</sup> Since fluctuations in final demand get amplified as one moves upstream along the supply chain, this provides an alternative explanation of the magnified fall in trade compared to GDP.

Due to the data limitations highlighted in Section 2, most of the above-mentioned studies have relied on indirect measures to evaluate the role of vertical specialization on the trade collapse. In this section, we will use data on China’s processing trade regime to evaluate if there is direct evidence of a compositional effect, trade cost effect and bullwhip effect in GPNs during the Great Recession.

The dataset that we will use in this section differs from the rest of the paper in an important way. Instead of using annual data, we will rely on processing trade data for the first quarter of 2008 and the first quarter of 2009. Since the Great Recession hit China’s exports in the last quarter of 2008, the quarterly data allow us to analyze the initial impact of the Great Recession on China’s processing trade. As it is shown in Table 8, the initial impact of the crisis was huge. In the first quarter of 2009, demand for China’s exports experienced a stunning contraction of 19.9% compared to the previous year, from US$304 billion to US$243 billion. We now turn to the analysis of the three effects.

> 20 Mason-Jones and Towill (2000) provide the following explanation of a bullwhip effect: “If demand for products is transmitted along a series of inventories using stock control ordering, then the demand variation will increase with each transfer”.

29
is available through the gravity portal of the US ITC.<sup>6</sup> For further robustness checks, we also use WIOD.

While Release 2 of the ITPDE includes trade data for manufacturing and agriculture since 1989, information on services is only available starting in 2000. Hence, our sample spans the years 2000 to 2015, a time crucial for the development of RTAs: According to the WTO, the number of RTAs in force more than tripled in this period.<sup>7</sup> For computational ease we restrict the sample to the 120 largest countries measured in terms of GDP in 2019 taken from the World Bank’s World Development Indicators.<sup>8</sup> To estimate Equation 4, we further need information on the presence of RTAs and their type. For partial scope agreements, free trade agreements, and customs unions, we draw information from Mario Larch’s RTA database (Egger and Larch 2008). For non-reciprocal arrangements the database on Economic Integration Agreements maintained by Jeffrey Bergstrand and Scott Baier is the main source (Bergstrand et al. 2015), we update it to 2014 ourselves using information from the WTO’s PTA database.<sup>9</sup> With these two data sets at hand, we know whether there was any RTA in force in the first place and we can distinguish between agreements that were notified under the Enabling Clause, i.e. non-reciprocal trade arrangements and partial scope agreements, and those that were notified under Article XXIV, i.e., free trade agreements and customs unions.

Our analysis builds on the World Bank’s Deep Trade Agreement Dataset (DTA data) provided by Hofmann et al. (2019) to determine which Article XXIV agreements can be considered to be “deep”. The data set on the content of RTAs maps 52 provisions in 279 PTAs notified to the WTO and signed between 1958 and 2015. It also includes information about the legal enforceability of each provision. We define agreements as deep when they cover more than 20 provisions, hence, the variable _deepijt_ equals one if a trade agreement covers more than 20 provisions and zero otherwise, _shallowijt_ is one if at most 20 provisions are covered. The richness of the data allows for distinguishing between the simple count of all provisions and those that are legally enforceable. For the second type of depth measure, we classify trade agreements to be deep when they contain at least 20 legally enforceable provisions. These definitions are comparable to Hofmann et al. (2019) and Mattoo, Mulabdic, et al. (2022).

One drawback of the DTA data is their coverage: only agreements that are still in force in 2015 are included. This is mostly an issue for deepening agreements as the shallower ones

> 6 https://www.usitc.gov/data/gravity/itpde.htm

> 7 http://rtais.wto.org/UI/PublicMaintainRTAHome.aspx.

> 8 The World Bank’s World Development Indicators are available at https://databank.worldbank.org/source/ world-development-indicators, we use GDP, constant 2010 US$ (time series: NY.GDP.MKTP.KD).

> 9 http://ptadb.wto.org/.

12
# **How Much Will the Belt and Road Initiative Reduce Trade Costs?**<sup>**1**</sup>

François de Soyres, Alen Mulabdic, Siobhan Murray, Nadia Rocha and Michele Ruta World Bank JEL Code: F14, F15, R41 Keywords: Transport Infrastructure, GIS Analysis, Shipment Times, Trade Costs 1 We thank Alan Deardorff, Michael Ferrantino, Caroline Freund, David Laborde, Mathilde Lebrand, Aaditya Mattoo, Chunlin Zhang, and seminar participants at the World Bank for helpful suggestions and Tristan Reed and Sasha Trubetskoy for their help in gathering information about transport infrastructure linked to the Belt and Road Initiative. Errors are our responsibility only.

Disclaimer: 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.
41 I/2905 issued in May 2014 exempted certain residential consumers from subsidy reduction. Criteria for exemption include low income, disability, being recipients of certain welfare benefits, and running business from home. Tariffs for all consumer categories were raised again in May 2015 (Table 5).

**Table 5: Revised natural gas tariffs effective May 2015 before tax with incentives for consumption reduction**

|Category|Reductio<br>Pesos/m<sup>3</sup>|n > 20%<br>US$/mcf|Reducti<br>Pesos/m<sup>3</sup>|on < 5%<br>US$/mcf|
|---|---|---|---|---|
|Residential R1|0.14|0.45|0.48|1.52|
|Residential R3 4|0.25|0.78|1.96|6.20|
|General Service P3|0.22|0.69|0.45|1.42|

_Source:_ <u>http://www.enargas.gov.ar/Tarifas/Index.php</u> _<u>.</u>_ _Note_ : The tariffs are for the Capital Federal region. Consumers in R1 are charged the least and those in R3 4 are charged the highest tariffs. The tariff for P3 is for the first 1,000 m<sup>3</sup> , with declining tariffs thereafter.

# **Bangladesh**

After four successive price increases in 2011, the government last raised liquid fuel prices in January 2013 (ww.bpc.gov.bd/). The only exception is jet kerosene, the price of which has been adjusted more frequently. Energy‐related subsidies declined as a percentage of GDP from 1.7 percent in FY 2013 to 1.0 percent in FY 2014 (July 1, 2013 to June 30, 2014) and 0.8 percent in FY 2015 (IMF 2014d).

Natural gas tariffs in Bangladesh have been regulated at very low levels. The tariffs were not adjusted between 2009 and September 2015—except the tariff for compressed natural gas (CNG) for automotive use, which was raised twice in 2011. The 2015 tariff increase did not affect fertilizer and power plants, which account for nearly half of the total gas consumption, and they continue to pay a mere US$1 per mcf (Table 6). These low prices have led to abandonment of some very large gas development projects ( _Financial Express_ 2015a), exacerbating gas shortages.

**Table 6: Natural gas tariffs in Bangladesh**

|Consumer category|Units|Taka|US$|
|---|---|---|---|
|Residental, double‐burner stoves|per month|650.00|8.35|
|Residential, single‐burner stoves|per month|600.00|7.71|
|Residential, metered|per mcf|198.22|2.55|
|Captive power plants|per mcf|236.73|3.04|
|Power plants|per mcf|79.85|1.03|
|Fertilizer|per mcf|71.36|0.92|
|Industrial users|per mcf|190.85|2.45|
|Tea estates|per mcf|190.85|2.45|
|Commercial users|per mcf|321.68|4.13|
|Compressed natural gas|per mcf|991.08|12.73|

_Source: Financial Express_ 2015b _. Note_ : Taka per cubic meter converted to taka per mcf.
**<u>Table A.3. RDD regressions of employment of individuals using VHLSSs 2004 to 2008</u>**

||||Dependen<br>|t variables<br>|||
|---|---|---|---|---|---|---|
|Explanatory variables|Currently<br>working<br>(yes=1, no=0)|Self-<br>employed<br>farm work<br>(yes=1, no=0)|Self-<br>employed<br>non-farm<br>work (yes=1,<br>no=0)|Having wage<br>job (yes=1,<br>no=0)|Log of<br>monthly wage<br>(wage<br>workers)|Log of<br>monthly wage<br>(all workers)|
||(1)|(2)|(3)|(4)|(5)|(6)|
|Program|0.0461***|0.1172***|-0.0340***|-0.0371*|0.1427*|-0.6372**|
||(0.0160)|(0.0314)|(0.0106)|(0.0201)|(0.0814)|(0.2508)|
|(Poverty rate – 50)|0.0008|-0.0081**|0.0035**|0.0054**|-0.0054|0.0548**|
||(0.0019)|(0.0038)|(0.0015)|(0.0022)|(0.0069)|(0.0254)|
|Program * (Poverty rate – 50)|-0.0016|0.0082**|-0.0035**|-0.0063***|0.0004|-0.0445|
||(0.0021)|(0.0040)|(0.0015)|(0.0023)|(0.0077)|(0.0281)|
|Age|0.0392***|0.0274***|0.0039***|0.0078***|0.0482***|0.1250***|
||(0.0015)|(0.0013)|(0.0005)|(0.0007)|(0.0075)|(0.0078)|
|Age squared|-0.0005***|-0.0003***|-0.0000***|-0.0001***|-0.0006***|-0.0016***|
||(0.0000)|(0.0000)|(0.0000)|(0.0000)|(0.0001)|(0.0001)|
|Male|0.0111**|-0.0288***|-0.0071*|0.0470***|0.0605**|0.9283***|
||(0.0054)|(0.0069)|(0.0037)|(0.0046)|(0.0264)|(0.0580)|
|Ethnic minorities (yes=1, Kinh=0)|0.0480***|0.2035***|-0.0761***|-0.0794***|-0.1935***|-0.5107***|
||(0.0106)|(0.0243)|(0.0106)|(0.0149)|(0.0433)|(0.1390)|
|District fixed effects|Yes|Yes|Yes|Yes|Yes|Yes|
|Year fixed effects|Yes|Yes|Yes|Yes|Yes|Yes|
|Constant|0.1671***|0.0978***|0.0496***|0.0196|6.5815***|-0.3888*|
||(0.0330)|(0.0362)|(0.0118)|(0.0194)|(0.1378)|(0.2099)|
|Observations|41,780|41,780|41,780|41,780|7,773|41,780|
|R-squared|0.266|0.154|0.048|0.050|0.073|0.078|

Note: This table reports district fixed-effect RDD regressions of employment of individuals using household-level observations. Robust standard errors in parentheses. Standard errors are clustered by district and village-year levels. *** p<0.01, ** p<0.05, * p<0.1 53
FIGURE 18.

# TRENDS IN INFANT MORTALITY COMPONENTS AMONG THE RURAL POOR IN RURAL COTE D'IVOIRE, 1970-86

<!-- Start of picture text --> 2/<br>L I~~~~~~~~~~~<br>P<>POO-NNNIt<br>NNMR NEONATAL -PMMRPOSlNEONATAL2/<br>Is -- -<br>-.<br><!-- End of picture text --> pp~~~~~p NOTE: (1) IMR6 - YEAR MOVING AVERAGE NOTE: (2) POOR - PODREST 60 PERCENT
March 1998, before PROGRESA was introduced to treatment communities. The March survey included a fairly detailed expenditure survey.

This paper employs household characteristic data from the November 1997 survey and an expenditure aggregate constructed using the March 1998 survey.<sup>11</sup> While it would be possible to undertake the analysis using income data from the November survey, the expenditure data is preferred for two reasons. First, the income data is very noisy. A substantial fraction of households report no income at all, and the income data shows no correlation with the March expenditure aggregate. The March expenditure aggregate, in contrast, is highly correlated with an expenditure aggregate from the June 1999 survey (for control group households), suggesting that it is a fairly consistent measure of household welfare. Second, the applications of the ELL methodology thus far have most commonly used household expenditure or consumption as the basis for welfare analysis, following the consensus that given the potential for consumption smoothing, consumption is likely to be a better indicator of long-term welfare than income. While it would be preferable to have expenditure data collected at the same time as household characteristics data, the household variables used here are unlikely to change substantially over time. Consequently the time gap between the November and March surveys should not distort the analysis.

While detailed, the expenditure aggregate is less comprehensive than typical consumption aggregates developed from some surveys carried out in developing countries. It covers only cash expenditures and does not include figures for rent. The expenditure survey was not carried out in 14% of households interviewed in November 1997. These households, which are concentrated in a small number of communities, are not included in the analysis. The ten communities with fewer than 10 households with expenditure information are also not included, leaving 20544 households in 496 communities.

> 10 A third potential source of error is associated with computation methods.  Elbers et al (2002) show that this can be set arbitrarily small by selecting a sufficiently large number of simulations.

> 11 Most questions in the November 1997 survey were similar to those in the 2000 national Mexican census. They concerned household characteristics and recent income of the household.

8