rafmacalaba/datause-encoder-data huggingface dataset:
# **3.2 Evidence on the certification process**

A detailed description of the size of different types of land and the certification process for each of the 529 sample villages is provided in table 2. The average village area is 12,790 mu (8 km<sup>2</sup> ). Certificates for collective construction land were issued to the village whereas those for contracted arable and forest land and residential land and actual structures were awarded to households.

Regarding implementation, we note that in more than 80% of cases, rules were made at the village level, either by the assembly (44%), economic organizations (23%), representatives (13%) or leaders (2%). Organization came more often from above (44% of township or above; 27% village leaders), and actual measurement was done by village representatives in 44% of cases.

In about 50% of villages, land registration gave rise to disputes and, where this was the case, an average of 11.1 disputes per village emerged. Disputes was most pervasive for arable and forest land (which attracted disputes in 45% and 31% of villages with 9.4 and 8.9 disputes, respectively) and least frequent with regard to collective and construction land (18.5% and 19.6% of villages with a mean of some 6 disputes). Even where disputes emerged, most of the cases encountered were resolved by village institutions: in villages with conflict, a total of 0.9 cases required intervention by institutions above the village.

After certification, contracts longer than 30 years were issued for all construction land and more than 95% of all other land use types with the exception of arable land (87%). Permanent land use contracts were given in close to 80% of cases overall, from 91% of residential and construction land to 84% of collective land, and some 58% and 59% of arable and forest land. Survey data point toward total cash cost of about Y 16 per mu of which close to half (43%) was contributed by the village and the remainder from outside. Villagers contributed close to 2,000 man-days of labor (about 3 days per household) and, with somewhat more than 10 person-months of labor by outsiders, contributions from above the village remained limited.

# **4. Econometric results**

Our estimates point towards significant reform-effects on land and labor markets. Reform-induced increases of tenure security: significant reductions of land reallocations and, to a lesser extent, expropriations seem to be a key driver. While reforms did not affect the amount of unused land, they triggered land transfers from ‘other’ to agricultural use and from residential to non-residential construction land with reform effects estimated to have been larger closer to Chengdu city center. Large part of observed land use changes was mediated through land markets, suggesting that reform efforts to improve transferability of land and reduce the transaction costs of land markets operation did have an impact. Beyond this, a significant increase in new enterprise startups may point towards independent impacts from labor market reforms.

11
# **1.       Introduction**

After the complete destruction of the agricultural labor market by disasters, rural households suddenly lose jobs and need to consider how they reallocate their labor between farm and off-farm employment. In such situation, it is essential to restore the agricultural sector to move underemployed households back to work, but investments in the non-agricultural sector may also help reduce rural poverty (Lanjouw and Lanjouw, 2001; Foster and Rosenzweig, 2004). Whether the economy reverts back to the pre-disaster situation or is transformed to a new structure could be driven by the relative aid effectiveness on farm and non-farm growth after the shock.<sup>i</sup> This paper considers the recovery process of the fishing villages in Aceh, Indonesia after the 2004 Indian Ocean tsunami. Following the almost complete destruction of production assets in Aceh, there was a huge influx of humanitarian relief (such as housing and fishing boats) and a reconstruction boom to restore destroyed public infrastructure, funded by the Indonesian government and international agencies. During this recovery process, the share of fishing sector fell, accompanied by a temporary expansion of non-fishing sector as shown in Figure 1.

My main theme is how aid _quality_ constrains the well-being of households after natural disasters. A few recent papers have examined the effectiveness of in-kind aid transfers on jobs, but the results are rather mixed.<sup>ii</sup> In Aceh, the in-kind transfer programs experienced a major challenge in trade-offs between aid quality, aid quantity, and the speed of delivery (Henderson and Lee, 2012; Nose, 2013). In particular, fishing boats from aid agencies were made of low quality materials or were improperly constructed due to a lack of quality monitoring by NGOs, shortage of qualified boat builders, a rush of boat orders with unrealistic delivery times, and limited amounts of resources (FAO, 2005).<sup>iii</sup> Due to the imperfect credit market, such quality shocks created a sizable income loss for those who were heavily affected by the tsunami.

Using household-level panel data, this paper provides rigorous evaluations of the short-term and long-term impacts of in-kind aid quality on fishermen’s job recovery and income growth after the tsunami. It further considers whether an alternative form of disaster-relief (i.e., the development 2
# **1. Introduction**

Studies in high-income countries have shown preprimary education provided to children between the ages of 3 and 6 has high returns both in small-scale interventions like the Perry Preschool Project (Heckman et al., 2010) and larger-scale government programs like childcare expansions in Norway (Havnes & Mogstad, 2011) and the Head Start program in the United States (Carneiro & Ginja, 2014; Kline & Walters, 2016; Bailey et al., 2020b). Studies have also estimated gains in cognitive and social emotional skills following modifications to curricula and pedagogy in existing preprimary classrooms (Barnett et al, 2008 and Clements et al, 2013) or changes in teacher quality (Araujo et al, 2016). In a comparative welfare analysis of 133 policies in the United States, Hendren and Sprung-Keyser (2020) find that investments in health and education for low-income children pay for themselves in the long-run.

Recent global evidence also shows a strong positive association between participation in preprimary education and child development measures, and this relationship is even stronger in low- and middle-income countries (McCoy et al, 2021). Evaluations in low- and middle-income countries also demonstrate sizeable improvements in skills and subsequent educational attainment following preschool interventions that expand access to preprimary education or improve the quality of existing programs (Berlinski et al., 2008; Martinez et al., 2017; Ganimian et al., 2021; Dean & Jayachandran, 2020). Yet, while the world has nearly reached universal primary education, coverage of early childhood education is not universal in many high and middleincome countries and falls below 20 percent on average in low-income countries (UIS, 2018).

Determining whether preprimary education investments are falling short needs to factor in both the benefits as well as the costs of such programs. To date, there has been no global metaanalytical study that aggregates estimates of causal impact for preprimary education or consistently calculates benefit-cost ratios of preprimary interventions in low- and middle-income countries. This review uses a multidisciplinary body of experimental and quasi-experimental evidence on preprimary education to estimate (i) the effect of expanding access or improving quality of preprimary education, separately for studies in high-income countries and studies in low- and middle-income countries, and (ii) benefit-cost ratios based on studies in low- and middle-income countries that report the per-child costs of the interventions under evaluation. Drawing on 798 effect sizes from more than 50 studies conducted in 19 countries, we examine 2
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19
In column 3 of Table A1, we consider an alternative definition of sustained poverty reduction that smooths out short term increases in the poverty rate. This alternative definition is equal to one in instances of sustained poverty reduction as defined by our baseline measure, but is also equal to one if the poverty rate has fallen by at least 5 percent between the first and last years of the fiveyear window. The market size variables are similar to those in column 1, but the threshold market size falls to 126 million people, as expected because the alternative measure is less demanding in classifying instances of sustained poverty reduction. This result suggests poverty reduction can be achieved with a smaller market size, though that it may not be sustained in all periods, as our baseline outcome variable requires.

Column 4 in Table A1 examines the implications of using higher frequency household surveys. This specification includes only surveys in which 0, 1 or 2 years of poverty headcounts are observed, reducing the sample to 200 observations. The signs and statistical significance of the estimated coefficients are robust to using this smaller sample, but the magnitudes change. The main takeaway from these results is that the inclusion of surveys with many missing observations for poverty does not push the estimates in a qualitatively different direction.

Columns 5 and 6 in Table A1 report results from specifications that have a weaker link to the theoretical framework. In column 5, the domestic middle class variable is lagged by 5 years to address potential concerns about reverse causation. Note that the middle class in our baseline specification is measured at the onset of each poverty-reduction-window, so by construction, it is not contemporaneous to poverty change. By using its lag (i.e., measuring it at the onset of the previous 5-year window), we lose 5 years for each country, so that we end up with 285 observations. The results from this specification are similar to those in column 4, in the sense that the coefficient signs remain robust, but the magnitudes change. The standard errors of the key variables become slightly larger due to the lower number of observations. In column 6, we include in addition to the variables suggested by the theoretical framework, initial (in 1981, the first year in our sample) log GDP per capita, to see if there is evidence of conditional convergence in the data. The coefficient on log GDP per capita is insignificant. The remaining results become – if anything - stronger than before, in the sense of being even more supportive of the mechanisms postulated by the theory, but the magnitudes are too large to be plausible and are hard to interpret given that the theoretical model has no implications for (conditional) convergence or divergence. In general, the results in specifications 5 and 6 are qualitatively similar to those in our baseline specification, but given that both specifications have a weaker link to the theoretical framework, we do not attempt to draw any quantitative conclusions from them.

23
# Figure 1: U.S. tariffs introduced in 2018

<!-- Start of picture text --> (A) Applied tariffs in the United States (B) Share of imports affected by new tariffs<br><!-- End of picture text --> <!-- Start of picture text --> Percent Average Percent<br>14 September 2018 14<br>Under consideration<br>12 12<br>10 10<br>8 8<br>6<br>6<br>4<br>4<br>2<br>2<br>0<br>0<br>United States China Global<br>Source: USITC, World Bank<br>A. Trade weighted averages.<br>B. Denominator reflects goods imports only. Tariffs implemented as of September 2018.<br>1940 1950 1960 1970 1980 1990 2000 2010 2018<br><!-- End of picture text --> implemented by Canada and Mexico on U.S. agricultural exports in response to U.S. steel and aluminum tariffs will reverse the modest export gains from the newly negotiated USMexico-Canada Agreement (USMCA). Analyzing a scenario of a U.S. trade war with China and Mexico, Bouet and Laborde (2018) find that trade wars will not improve U.S. welfare and will harm China and Mexico as well as the global economy. Rutherford et al. (2018) estimate that the welfare costs of a trade war could be substantial, with losses concentrated in the United States and China, and small effects on other countries. Likewise, Zandi et al. (2018) establish that potential global trade wars will entail losses in U.S. GDP and jobs. If the trade tensions raise global uncertainty and lead to depressed investments in developing countries, Freund et al. (2018) estimate that the income losses in developing countries could range between 0.9 percent for South Asia and 1.7 percent for Europe and Central Asia.

Adding to the current literature, this paper examines the effects of alternative policy options for countries in to the escalation of the trade between developing response dispute the United States and its trading partners. As the exact nature of the current trade tensions is still evolving, we devise four different hypothetical counterfactual trade war scenarios 2
# **3. Methodology**

We propose a methodology which enables comparison among various existing international and regional assessments. We obtain a _Harmonized Learning Outcomes_ (HLO) database, which is comparable over a set of 163 countries / areas form 1965-2015. The foundation for our approach is to index across a given pair of achievement tests with results from countries that participate in both. To link results over time, we perform a similar procedure using the United States as an anchor since it has participated in all IEA assessments since 1965 as well as a consistently administered national assessment, the _National Assessment of Educational Progress (NAEP)_ . Similarly, we use results from the national assessment conducted in Burkina Faso to anchor PASEC results over time. First, we present methodologies which can be used for anchoring assessments. Then, we show how we obtained the final anchored dataset.

# _3.1 Linking Methodologies_

Various methodologies can be used for linking or equating assessments. Equating is a statistical process that is used to adjust scores on tests so that scores can be used interchangeably (Kolen and Brennan, 2014). The purpose of equating is to adjust for difficulty among assessments that are built to be similar. In our case, assessments are not directly comparable since difficulty and content may differ. Instead, we use a similar approach to equating, known as _scaling to achieve comparability_ according to the _Standards for Educational and Psychological Testing_ (AERA, APA, NCME, 1999). This is also known as _linking_ in the terminology of Holland and Dorans (2006), Linn (1993) and Mislevy (1992). As explained in Kolen and Brennan (2014), similar statistical procedures are used in linking and equating, although their purposes are different. In this paper, we use the terminology of _linking_ instead of _equating_ since the tests we link used are purposefully built to be different. Notably, we do not link using Item Response Theory (IRT) – the technique used to generate scores for each respective international and regional assessment. IRT models the probability a given pupil answers a given test item correctly as a function of pupil and item-specific characteristics. While this methodology is used _within_ each of the international and regional tests we use, to use it _across_ ISATs and RSATs would require overlap in test items. This is not true for a significant enough tests and time intervals to create a globally comparable panel dataset. Moreover, even when there is overlap, for IRT to be reliable there must be a large enough instance of item-specific overlap. When this overlap is small, standard maximum likelihood estimates will reflect both true variance and measurement error, overstating the variance in the test score distribution. Das and Zajonc (2010) elaborate on the various challenges of estimating IRT parameters with limited item-specific overlap.

12
owned enterprises. It includes direct expenditures on infrastructure and equipment in all sectors, donor-financed projects and the state’s external borrowing on behalf of the private sector. Current expenditures are expenses under Tunisia’s _Titre 1_ , i.e, salaries and wages, goods and services, interest payments and transfers and subsidies. In this paper, we exclude interest payments from recurrent expenditures. Private investment is measured as the gross fixed capital formation by the domestic private sector.

Both recurrent expenditures and GDP are converted to real terms by using the GDP deflator. Public and private investment variables are adjusted by the deflator of investment (base 2000) from both the _Institut National des Statistiques_ and the World Development Indicators. Because the deflators for 2006 and 2007 were missing in both databases, we approximated them by assuming that the deflator has changed at the same rate as on average in the period 2000-2005.

# **_3.3. Unit roots and co-integration tests_**

Tables 2 and 3 in annex show the results of the unit root tests. They show that all the variables in the system have a unit root in level but are stationary in first difference. We then apply the Johansen (1988 and 1991) and Johansen and Juselius (1990 and 1992) co-integration tests.<sup>4</sup> As Table 4 shows, both tests indicate that the null that there is no co-integration relationship between the two variables (r=0) is rejected at 5 percent. On the other hand, one cannot however reject the hypothesis that there is _one_ co-integration relationship (r<=1) against _r=2_ . An SVEC model is thus the correct specification.

# **_3.4. Impact of fiscal shocks –impulse responses_**

_Restrictions imposed on short-term multipliers_ For the multiplier matrix to be identified, some assumptions should be made regarding the contemporaneous relationships between the variables of the system. In our case, we have four variables and have imposed the following restrictions in the SVEC short-term multiplier matrix based on economic theory and specific institutional constraints (see Table 5):

- Output does not affect public investment or recurrent expenditures instantaneously. This assumption may be seen as strong a priori because we use annual data and Tunisia does undertake revised budget laws from time to time (twice in the 1990s and 4 times since

> 4 In the Johansen framework, this a full information maximum likelihood estimation of a system characterized by П co-integrating vectors.

7
24

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