rafmacalaba/datause-encoder-data huggingface dataset:
that international rules can be consequential when they form part of a dominant long-term strategy for state actors. Institutionalism resembles realism, however, in its largely pessimistic view of the likely effects of human rights treaties, which are unlike trade and environmental treaties, in which states that comply can expect reciprocal behavior from other countries. States have no long-term interest in complying with human rights regimes, apart from possible reputational effects.

Some empirical work on the impact of human rights treaties is consistent with these perspectives. Hathaway, using data from State Department country reports, Freedom House data, and the InterParliamentary Union, finds that ratifying countries have the same or lower ratings for genocide, torture, fair trial, civil liberty, or women’s political participation (Hathaway 2002). Hafner-Burton and Tsut **s** ui (2004) regress the level of government repression (scaled 1 to 5) on a lagged dependent variable, treaty ratification, and some control variables and find that treaty ratification does not reduce rates of torture or repression, particularly in the worst offenders. Neumayer (2005) similarly estimates civil and personal integrity rights as a function of treaty ratification (European Convention for the Protection of Human Rights, European Convention for the Prevention of Torture, American Convention on Human Rights, Inter-American Convention to Prevent Torture, and the African Charter on Human and Peoples’ Rights), and finds that “rarely does treaty ratification human rights.” Although some of these papers recognize the endogeneity of treaty ratification, none uses an instrumental variable approach. Simmons (forthcoming 2009) does use an IV approach to estimate the impact of ratifying the CRC on measles and DPT immunization rates and finds that treaty ratification may have had some small effect on measles but not on DPT coverage rates (her approach is described in more detail below).

There are certainly reasons for skeptics to expect that the CRC likewise has little real world impact. The treaty is not enforceable in any powerful sense of the word. In a parallel fashion with other human rights conventions, the CRC did establish a Committee on the Rights of the Child to oversee implementation on the part of signatories and to encourage international cooperation. State parties are required to develop National Plans of Action and periodically report to the Committee. NGOs and civil society actors occasionally alternative reports to the committee, and participate in the review (and 4
8 being covered by HCFP. A treated individual’s outcome is compared with a counterfactual outcome, formed as a weighted average of the outcomes of untreated individuals, where the weights reflect the propensity scores, the exact weighting scheme depending on the variant of PSM used (discussed below). The differences are then averaged to get the average treatment effect (on the treated).<sup>7</sup> This approach ensures that account is taken of the fact that households selected for HCFP coverage differ in a variety of observable respects from those not selected; failure to take this into account would result in biased estimates of the impact of HCFP. Individuals in the ‘treated’ and ‘untreated’ groups who are too dissimilar from the other group are discarded, and the focus is on a subsample for which good matches can be found for the treated individuals in the untreated group. What this approach does _not_ do is to take into account the possibility that individuals are selected in part on the basis of _unobservable_ variables and these variables also influence outcomes. As indicated in the Introduction, the frequently used approach of double-differencing with panel data and sweeping out time-invariant unobservable variables is not an option in this case, since it requires that the program has not yet been implemented in the baseline, and the only survey that could serve as a baseline (the 2002 VHLSS) was undertaken after the precursors to HCFP has already started.

Are there reasonable grounds for believing there to be selection into HCFP on unobservables? And are the likely biases likely to be large? Certainly, there are stories one could tell. Ethnicity is, of course fixed, at least in principle, and cannot be influenced by unobservables that also influence out-of-pocket spending and health utilization. But it might be _correlated_ with such unobservables. The same is true of whether or not someone lives in a commune covered by Decision 135. Which direction such unobservables bias the estimated impact of HCFP is unclear. In the case of poverty status, the direction of bias seems clearer. In this case, the indicator determining eligibility could indeed be influenced by unobservables. Local officials may be tempted to err on the side of including a near-poor household that is known to have a history of high medical

> 7 For excellent reviews of the recent impact evaluation literature, see Imbens (2004), Blundell et al. (2005) and Ravallion (2005). For a useful practical guide to PSM, see Caliendo  and Kopeinig (2005).
fact Asia had large resources of primary materials and a significant technological base from which to produce goods that were highly desired in Europe.

# **Asia's Historical Place in the Trading World**

Trade between Asia and Europe began over 2,000 years ago (5,000 according to some) and increased after the 16'h century with the establishment of direct maritime contact.<sup>31</sup> More precisely, the opening of the direct sea route around the Cape of Good Hope led to the integration of global trade generally between 1500 and 1800 with the Portuguese pioneering direct European maritime trade with Asia.<sup>32</sup> In the 16th century the Portuguese were a dominant presence in Euro-Asian trade. Their position, however, was successfully challenged in the 1 7<sup>thand1</sup> **8**<sup>**th**centuriesby other Europeans,particularly</sup> the Dutch and the English who founded joint-stock companies specifically to trade with Asia (i.e., the Dutch Verenigde Oostindische Compagnie (VOC) and the English East India Company (EIC).) The shift in dominant European presence in Asia among these three countries from the 16'h through the 18'h centuries is demonstrated in Table 1.5.

## Table 1.5

|NumberofShipsSailingtoAsiafromSe|venEuropeanCount|ries,1500-1800|
|---|---|---|
|**1500-99'**|**1600-1700**|**1701-1800**|
|Portugal<br>705|371|196|
|<br>Netherlands<br>65|1,770|2,950|
|England|811|1,865|
|France|155|1,300|
|Otherb|54|350|
|Total<br>770|3,161|6,661|
|**'1**590sfortheNetherlands|||
|b'Other'referstoshipsofthe Danish, Swedishtrading com|panies,andthe OstendCom|pany (Austria).|
|Source: Maddison (2001:Table2-6,**63)**sourced originallyf<br>inBruinandGaastra(1993:7and17);otherwisefromBruij|rom:Portugal1500-1800from<br>nandGaastra(1993:178an|MagalhAesGodinho<br>d183).|

While the English expanded their presence between the 17th and 18th centuries, the Dutch retained the largest maritime presence among Europeans in both centuries. The presence of the Portuguese declined to almost nothing in the **18th** century.

From 1400 to 1800, Asia-related trade can be conceptually divided into two spheres: intra-Asian and global. The intra-Asian trading sphere can be further divided into two overlapping regions: the Indian Ocean region (encompassing the Middle East, Central Asia, India, and Southeast Asia) and the Asian region (encompassing Central Asia, India, and East Asia).<sup>33</sup> During the period under discussion, goods produced and traded by Asia included a wide variety of luxuries and commodities, with some of the most prominent being pepper, spices, sugar, silk and cotton textiles, rice, wheat, sugar, coffee, opium, precious stones, medicines, weapons, and horses. Another commodity that played a key role in Asia-related trade was precious metals (especially silver).

8
in the next section. Section 3 provides a description of the data collected; Section 4 presents our results. Section 5 concludes.

# **2. The survey experiment**

Whether changes in the measurement method have an effect on the statistics they produce is, ultimately, an empirical question. We designed and implemented a survey experiment in Tanzania focusing on two key dimensions of labor survey design: the inclusion of screening questions in the questionnaire with respect to identifying labor force participants and the type of respondent. In this experiment, we have two different questionnaire designs (which we call “detailed” and “short”) and two respondent types (proxy and self-report). Households were randomly selected for the survey from seven districts in Tanzania; we describe the household selection process in the subsequent section. After households were selected within the village, they were randomly assigned to one of four groups defined by the combination of the two experiments, one orthogonal to the other: detailed and self-report, detailed and proxy, short and self-report, and short and proxy. Details on the sampling approach and survey assignment for households and individuals are provided in Section 4.

The experiment was conducted for both adults and children—individuals eligible for data collection were all those age 10 and older. In this paper, we focus on the responses from children and the measurement of child labor. We define child labor as the labor force activity of a child ages 10 to 15 who has engaged in at least one hour of labor market activity over the past seven days. An internationally recognized definition of child labor remains an open item in the child labor policy agenda as current international agreements such as the ILO’s Convention 138 agree on age limits for child labor, but leave discretion to member countries on hours and activity restrictions in defining child labor. Our definition is consistent with the ILO’s Statistical Information and Monitoring Program on Child Labor (SIMPOC) definition of child labor.<sup>2</sup>

> 2 In another paper, we focus on the measurement of labor statistics for all the adult population (Bardasi et al., 2010). Note that the “adult labor statistics experiment” and the “child labor statistics experiment” on which we report in this paper are not separate experiments, but rather focus on two different populations in the same survey experiment.

5
**Table 3. Percent changes in poverty measures (MI-SI)**

|||$3.65<br>|||$6.85<br>||
|---|---|---|---|---|---|---|
||**H**|**PG**|**PG2**|**H**|**PG**|**PG2**|
|National|-7.02|-7.81|-11.87|-0.29|-1.21|-2.67|
|Urban|-15.24|-17.37|-23.60|-1.90|-5.04|-8.32|
|Rural|22.18|24.95|23.42|4.41|10.47|15.12|
|Tehran metro Urban|-32.93|-36.50|-47.41|-5.72|-13.12|-20.04|
|Caspian Rural|2.93|2.34|2.61|0.84|1.17|1.71|
|Caspian Urban|-5.51|-4.33|-3.47|-5.07|-3.04|-3.67|
|Northwest Rural|8.46|15.88|0.00|12.86|13.37|12.55|
|Northwest Urban|0.85|0.23|-1.34|3.15|1.57|1.61|
|Northeast Rural|84.53|87.78|118.75|14.26|31.86|45.17|
|Northeast Urban|-2.39|-3.19|-3.07|-0.03|-1.43|-1.92|
|Central Rural|21.79|23.17|19.16|1.63|8.54|12.65|
|Central Urban|-7.92|-9.87|-11.84|-1.83|-2.67|-4.36|
|Southeast Rural|24.96|30.06|29.50|0.55|10.06|17.11|
|Southeast Urban|1.10|-0.36|-0.98|0.88|0.03|-0.03|
|Persian Gulf Rural|20.24|28.48|30.32|6.51|11.66|16.36|
|Persian Gulf Urban|-0.46|0.45|-0.85|0.30|0.41|0.82|
|Zagros Rural|54.26|21.21|0.00|11.50|18.78|23.91|
|Zagros Urban|2.62|2.61|3.90|0.35|1.41|1.76|

_Source_ : Authors calculation based on HEIS 2019 Overall, differences in terms of poverty estimates between the two deflation approaches are sensitive to the value of the poverty line – in line with theoretical predictions (Figure 1). Moreover, given that spatial price indexes are defined at the region/area level and that biases in urban/rural areas would go in opposite directions, differences in poverty estimates the national level tend to be relatively smaller compared to the ones at the subnational level. Considering the $3.65 poverty line, the MI approach would result in a 7 percent underestimation of poverty at the national level, which is the composite effect of a 15 percent underestimation of poverty in urban areas and a 22 percent overestimation of poverty in rural areas, compared to the SI approach. At the higher value of the poverty line ($6.85), the bias at the national level is negligible, while poverty in urban (rural) areas still results underestimated (overestimated) when using the MI approach compared to the SI approach.

In urban Tehran, compared to single index deflation, the MI approach would result in a 33 percent (5.7 percent) underestimation of poverty at the $3.65 ($6.85) poverty line. In rural Southeast the MI 32
sign and significant at the 10% level in the restricted regression. This overall strong performance suggests that the poor results of home labor market variables in many previous studies arises precisely because they capture two contradictory tendencies.

# _Integration Variables_

Columns 2a, 3a, 4a and 5a drop the labor force variables and replace them with the trade and investment variables, again in relative and free standing form. In all cases, we find evidence of a strong substitution effect: FDI and trade reduce migration. The free standing term was significant in half the cases consistent with López and Schiff’s (1998) concern that trade and investment integration may plausibly increase migration flows by releasing liquidity/wealth constraints. In the case of maquilas and imports, it appears that this liquidity effect offsets to some extent the substitution effect found in the relative term.<sup>7</sup> Columns 2b, 3b, 4b, and 5b add the labor force variables and suggest that some, but not all of the effect of the trade and investment variables works through the labor market. This is consistent with Hanson’s (2005) finding that the distribution of conditional labor income in states highly exposed to very similar trade and investment variables were shifted to the right relative to states with low exposure. The substitution effect diminishes by at least a factor of 2 in most cases and in the case of FDI becomes insignificant. The exception is the maquila variable, which appears to strengthen. Whether this is due to the selection bias caused by the authorities grouping states with small maquila presence is not clear.

> 7 As additional robustness tests, we ran two additional variants of the base and FDI regressions.  We first include a full set of state dummies, both origin and destination. This had the predictable effects of the substantially reduced degrees of freedom, but had relatively little effect on the magnitudes of the core variables.  In the key specification on which we base our simulations, 2b, the relative FDI term changed little, falling from .029 to .021 and the t from 6.4 to 3.6.  The free standing term remained insignificant. Second, we include a measure of relative education levels measured as average years of schooling. The relative and free standing initial terms enter insignificantly and had little impact on the other covariates with the exception of a perhaps predictably lowering, somewhat, of the relative wage term and rendering insignificant the free standing amenities term.

11
per year, from birth to age five” and a control group (Currie 2001). At school entry, the study children were again randomized into two groups, one of which received no further intervention, and another which received a “Home-School Resource Teacher”. At age 15, the children who had received the preschool intervention had higher scores on achievement tests, and reductions in the incidence of grade retention and special education. (Children who are placed in a special education “track” are generally more likely to drop out of school in the future.) The effects of the Home-School Resource Teacher were either small or insignificant. At age 21, the children exposed to the Abecederian intervention had higher average test scores, and were twice as likely to be still in school or to have ever attended a four-year college.

The evaluations of the Perry Preschool Project and the Carolina Abecederian Project provide “laboratory” evidence of the possible returns to investments in early childhood. However, these “model” interventions are typically funded at higher levels and are administered by staff who are more motivated and better trained than staff at large-scale programs. Moreover, as in many clinical trials, the sample sizes in these evaluations are generally very small—less than 100 children in the treatment and control groups each. It is therefore important to complement these evaluations with analysis of the impact of Head Start, the largest program for disadvantaged preschool children in the United States.

Head Start, created in 1965 as part of the Johnson administration’s “War on Poverty”, provides disadvantaged children with (predominantly part-day) preschool programs. In 1999, the program covered 800,000 children—almost 50 percent of eligible three and four year-old children—and received $4.7 billion of federal funding (Currie 2001). There has never been a large-scale, randomized evaluation of Head Start, so evaluations have relied on a variety of techniques to construct comparison groups—for example, comparing children who attended Head Start with others who did not (Lee et al. 1990), comparing siblings who attended Head Start with those who did not (Currie and Thomas 1995), or comparing children in schools which offered Head Start for two years with those which offered it for three years (Reynolds 1998). These are serious attempts to correct for the potential endogeneity of participation in Head Start. However, the results may still be biased if self-selection into Head Start on the basis of unobservables is important—for example, if parents are more likely to enroll children who have learning difficulties or, alternatively, enroll promising children they expect would benefit most from the program (see Todd and Wolpin 2003 for a general discussion of these issues).

With this caveat in mind, the studies that are methodologically most sound generally report significant effects of Head Start. Children who attended Head Start are less likely to be enrolled in special education when they reach school, more likely to make adequate grade 6
# **Table 1: Terms of the Provincial Bank Privatizations**

|**Province**<br>**(Bank)**|**Object of**<br>**Sale**|**Branching**|**Employees**|**Duration of**<br>**Banking**<br>**Service**<br>**Contracts**|**Portfolio**<br>**Guarantees**|
|---|---|---|---|---|---|
|Chaco<br>(6/94)|60% Class A<br>shares|Maintain service|Keep at least 715<br>workers|20 years|None|
|Entre Rios (12/94)|60% Class A<br>shares|Maintain<br>service, closures<br>require approval|Up to 700 (of<br>1500) early<br>voluntary<br>retirement|7 years|Up to $26<br>million<br>maximum|
|Formosa<br>(9/95)|60% Class A<br>shares|Maintain service|--|10 years|35% recovered<br>residual assets|
|Misiones<br>(12/95)|100% Class A<br>shares||No dismissals in<br>first six months;<br><30% of<br>workforce after|5 years|Up to $16<br>million<br>maximum|
|Rio Negro*<br>(2/96)|Deterrnined<br>by bidders|||10years|Up to 80% of<br>portfolio or $50<br>million|
|Salta<br>(3/96)|75% Class A<br>shares|Maintain similar<br>geog. Coverage||10 years|None|
|Tucuman<br>(3/96)|75% Class A<br>shares|Maintain service|Workforce<=<br>200 at transfer|IO years|Up to $32<br>million|
|San Luis<br>(5/96)|100% Class<br>A,B shares|Maintain service|--|10 years|$16 million<br>deposit from<br>province, up to 5<br>years|
|Santiago del Estero<br>(7/96)|95% Class A,<br>B shares|Maintain service|Job re-training<br>rom<br>>1vr.|10 years|None|
|San Juan<br>(7/96)|75% Class A<br>shares|Maintain similar<br>geog. Coverage|--|10 years|None|
|Mendoza<br>(7/96)|90% Class A<br>shares|Maintain all<br>branches|Keep at least 600<br>workers|5 years|Can substitute p-<br>tized assets for<br>residual assets,<br>Upto $20 million|
|Mendoza<br>(Prev. Social)<br>(7/96)|90% Class A<br>shares|Maintain all<br>branches|Keep at least 500<br>workers|5 years|Can substitute p-<br>tized assets for<br>residual assets,<br>upto $10 million|
|Municipal de Tucuman<br>(10/97)|100% Class<br>A,B shares|Maintain service|Keep at least 70<br>workers|10 years|<br>Can shift some<br>assets to the<br>residual|
|Jujuy**<br>(1/98)|80% of<br>capital|Maintain all<br>branches|Keep at least 170<br>workers|10 years|Fund created w/<br>35% recovered<br>residual assets|
|Santa Fe<br>(5/98)|90% of class<br>A shares|Maintain service<br>in all branches<br>or through paid<br>representatives|Keep at least<br>1500 workers|5 years|Up to $43<br>million<br>guaranteed by a<br>bond|
|Santa Cruz<br>(6/98)|Not available|Not available|Not available|Not available|Not available<br>__I_I_I|

Source: Fondo Fiduciario para el Desarollo Provincial (FFDP)

*Rio Negro - Portfolio guarantees and flexibility with respect to the object of sale were modifications to original pliego. Pliegos were initial announcements by the provinces of the proposed terms of sale. ** Jujuy - The original pliego was altered to allow for a higher share of capital to be transferred to the new owner, less stringent restrictions regarding firing, and slightly more generous guarantees.

**10**
# **4. Services Sector Performance: Determinants**

In Section 3, we identified important differences in labor productivity levels and growth rates across services sub-sectors and countries within the ECA region. Understanding the determinants of these differences in performance is crucial for policy purposes. Some important factors that may explain differences in performance across sub-sectors are capital intensity, market size and the scale at which services can be sold, human capital, technological innovations (particularly the use of ICT), policies and institutions (van Ark et al., 1999). Due to data limitations we follow different approaches to examine the role of ICT, skills, and policy reforms for the performance of services in the ECA region. While we can only examine the role of ICT and skills through simple taxonomies, we can assess the role policy reforms through econometric specifications.

First, we assess the importance of ICT for the performance of services sub-sectors in ECA countries, relying on the taxonomy proposed by van Ark and Piatkowski (2004). A services sub-sector is categorized as an ‘ICT producer’ according to the OECD definition.<sup>23</sup> Alternatively, a services sub-sector is categorized as an intensive user of ICT (‘ICT user’) or as a non-intensive user of ICT (‘Non-ICT’) based on the ICT capital share of the sub-sector using the U.S. as a benchmark as in van Ark et al. (2003), given that data on ICT investment by sub-sector is not available for ECA countries. Appendix Table A.1 shows to which ICT category each of the NACE 2-digit services sub-sectors belongs. Unreported results show that ICT producers and ICT users exhibit substantially higher average KLEMS labor productivity levels than non-ICT sub-sectors in most EU-8 countries in 1997-2004.<sup>24</sup> Figure 12 shows average annual growth in KLEMS labor productivity across EU-8 countries in 1997-2000 and in 2000-2004 for each of the three ICT-related categories. For EU-8 countries overall, ICT users exhibit the fastest productivity growth in 1997-2000 while non-ICT sub-sectors exhibit the fastest productivity growth in 2000-2004. However, there is some heterogeneity across countries. In 2000-2004, ICT users experience the fastest productivity growth in all EU-8 countries except Latvia and Lithuania. In Hungary and Poland, ICT producers also

> 23 The OECD defines as ICT producers the sub-sectors which produce IT hardware, communication equipment, telecommunications, or computer services (including software).

> 24 This finding is valid when excluding real estate activities from the average productivity of non-ICT subsectors due to the aforementioned artificial over-estimation of labor productivity in this sub-sector. Note that it is impossible to classify the sub-sectors in the WIIW database into the ICT categories.

26