rafmacalaba/datause-encoder-data huggingface dataset:
skilled (Lazear, 2000) or, more pessimistically, the highly intrinsically motivated. Second, given the longer time frame, teacher characteristics could have changed. Experienced P4P may have eroded a given teacher’s intrinsic motivation (as hypothesized in the largely theoretical literature on motivational crowding out) or, more optimistically, encouraged a given teacher to improve her classroom skills. In this section, we conduct an exploratory analysis of these dynamic effects.<sup>35</sup>

**Retention effects** We begin by exploring whether experienced P4P affects retention rates among recruits. Specifically, we look for an impact on the likelihood that a recruit is still employed at midline in February 2017 at the start of the Year 2; i.e. after experiencing pay-for-performance in Year 1, although before the performance awards were announced. To do so, we use a linear probability model of the form

where _employediqd_ 2 is an indicator for whether teacher _i_ with subject-family qualification _q_ in district _d_ is still employed by the school at the start of Year 2, and _γq_ and _δd_ are the usual subject-family qualification and district indicators.

As the first column of Table 5 reports, our estimate of _τE_ is zero with a randomization inference _p_ -value of 0.96. There is no statistically significant impact of experienced P4P on retention of recruits; the retention rate is practically identical—at around 80 percent—among recruits experiencing P4P and those experiencing FW.

It is worth noting that there is also no impact of experienced P4P on _intentions_ to leave in Year 3. In the endline survey in November 2017, we asked teachers the question:“How likely is it that you will leave your job at this school over the coming year?”. Answers were given on a 5-point scale. For analytical purposes we collapse these answers into a binary indicator coded to 1 for ‘very likely’ or ‘likely’ and 0 otherwise, and estimate specifications analogous to equations (5) and (6). As the second column of Table A.5 shows, there is no statistically significant impact of experienced P4P on recruits’ self-reported likelihood of leaving in Year 3. Our estimate of _τE_ is _−_ 0 _._ 06 with a randomization inference _p_ -value of 0.40.

Of course, a retention rate of 79 percent implies 21 percent attrition from Year 1

> 35We emphasize that this material is exploratory; the hypotheses tested in this section were not part of our pre-analysis plan. That said, the structure of the analysis in this section does follow a related pre-analysis plan (intended for a companion paper) which we uploaded to our trial registry on October 3, 2018, _prior_ to unblinding of our data.

32
0.010 <u>p for endogeneity</u> Source: Village Fund Survey 2010 and SES 2009. Robust standard errors in parentheses. Variables in first column are included based on OLS backward stepwise with p=0.2 cutoff. Regression in second column includes provincial dummy variables (not shown). * p<0.05, ** p<0.01, *** p<0.001.

# **8. Cost-Benefit Analysis**

Do the benefits of the Village Fund outweigh the costs, from an economic point of view? That is the issue we address in this section.

The costs of VF lending may be separated into administrative and financial components. The most important administrative cost is the time spend by VF committee members; to some extent this is compensated in the honoraria that committee members pay themselves, which comes to 1.1% of the value of loans disbursed, and may even be overly generous in some cases. It may be appropriate to add the imputed value of volunteering – time spent working for the VF that receives no, or below-market, compensation. We have valued this additional time at 300 baht/day, in line with the average rural wage in 2009, although a case can be made that since the time was freely offered, this adjustment might not be needed.

Village Funds also make social contributions, such as helping pay for funeral expenses, that represent 0.5% of lending; we treat this as a cost, viewing it as the price of ensuring local goodwill. Other costs at the village level – stationery, even use of a computer – are very small. We do not have information on the cost of running the VF headquarters or regional centers, but this appears to be a relatively modest operation; if it costs $2 million annually, that would represent just 0.1% of the value of lending. Overall, administrative costs come to about 2% of total lending.

There is a cost involved in raising funds to lend to VF borrowers. Some of these costs are explicit – interest paid to the BAAC or GSP for loans, interest paid to households that make deposits in the VF, and dividends paid to those who buy VF shares. We assume that these capital costs are competitive with other financial institutions, and not excessive. It is possible that the interest and dividend payments to VF members are higher than necessary – a way of sharing the rent inherent in the VF – and so these numbers are likely to be upper bounds.

Local VFs were provided with an initial million baht, and in some cases additional amounts of 100,000 baht or more in subsequent years, without being required to pay an interest on these funds. A small number of Village Funds also received capital from NGOs. From an economic point of view, this capital does have an opportunity cost. We assume that the appropriate interest rate is the one that the BAAC or GSB charges 41
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While IRT might not be a reliable approach when there is limited item-by-item overlap, we conduct a few robustness tests where overlap is larger. We compare our results to the Linking International Comparative Student Assessment (LINCS) project which uses IRT methods and has significant overlap in items for a subset of international studies focused on reading at primary school from 1970 onwards (Strietholt, 2014; Strietholt and Rosén, 2016). If our expanded HLO database can produce similar results to original scores and IRT methods where there is overlap, we gain confidence in our results as well as an expanded dataset.

We note that while mean scores might vary by linking methods, and should be caveated appropriately, ranks and relative performance are relatively robust. While Sandefur (2016) finds large variation on mean scores depending on the equating method chosen, the Spearman rank correlations of the country averages are .97 or higher.

In building globally comparable education quality estimates, we rely on classical test theory (Holland and Hosken, 2003). Suppose that a population of pupils, sampled from the target population T, takes two different assessments X and Y. Here, we suppose that any differences in the score distributions on X and Y can be attributed entirely to the assessments themselves, since group ability is assumed to be constant.

The goal of linking is to summarize the difference in difficulty between two tests X and Y. We would like to link test X , the Anchored Test, to the scale of test Y, the Reference Test. For example, if we want to link PISA 2003 to TIMSS 2003, PISA 2003 is the Anchored Test X while TIMSS 2003 is the Reference Test Y.

Our main estimation method is ratio linking. To conduct ratio linking we index the difference in means in the Anchored Test X and Reference Test Y as follows: where 푙푖푛푘푖푛푔푌푝푙(푋) is the equation for converting observed scores on Anchored Test X to the scale of Reference Test Y. A limitation of this methodology is that it is sensitive to the scale of each test being similar. We address this potential limitation by using tests with a mean of 500 and standard deviation of 100.<sup>2</sup> This ensures that ratios capture differences in test difficulty rather than differences in scaling.

Below we specify each step in the process. The conversion rate is calculated as follows. Mean scores for tests X and Y, 휇(푋) and 휇(푌), are first calculated for a given round r, subject s and level l. We consider tests to be in the same round if they are five years apart and optimize to have the rounds as tight as possible. Most often this translates to within one to two years. In some cases, this extends to three to five years apart. In a few

> 2 In rare cases where tests do not have initial scores on this scale, we rescale the test using the microdata.

10
25

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probability of receiving program benefits when considering PMT-specific predictions for all SUSETI households, as opposed to UDB households only. This census scenario also leads to a slight reduction in leakage, as shown by the lower program receipt probability for households in the upper portion of the consumption distribution. Some of these improvements in targeting are of course a mechanical result due to the expanded inclusion of poorer households in the registry.

In Figure 7, we analyze an alternative scenario in which we conduct a full enumeration in the poorest half of districts of the sample and a UDB-based registration in the richest half. This less costly, quasigeographic targeting approach also yields some improvements in both undercoverage and leakage when compared to program incidence with actual UDB-targeted receipt. However, as expected, improvements in undercoverage under this middle scenario are slightly lower than with full census enumeration in all districts. For the Jamkesmas program, for example, the poorest households have a probability of about 65 percent of receiving the program under a complete full enumeration scenario. Under a scenario with full enumeration only in the poorest half of districts, this probability is about 10 percentage points lower. Furthermore, compared to the actual UDB, there is no significant change in leakage for both Jamkesmas and BLT under the partial census approach. Together, the results in Figures 6 and 7 point to the significant improvements in coverage among the poorest ten percent of households when moving to the full enumeration approach.

Nevertheless, we acknowledge that even under full enumeration, undercoverage appears high. This persistent targeting error points to two important limitations of any analysis relying on a static measure of expenditures as the main indicator of welfare. First, in a context where expenditures churn quite often, we may erroneously identify a household as more or less “eligible” for a given program when, in fact, their actual beneficiary status reflects superior local knowledge about dynamic welfare status.<sup>17</sup> Although this is an inherent shortcoming of studies constrained to use static targeting metrics, such high rates of churning make it difficult to develop a scheme that fully eliminates targeting errors.

> 17 Churning around the poverty line is pervasive across Indonesia. Although the poverty rate is just above 10 percent nationally, the operating definition of “poor and vulnerable” households extend up to the 40<sup>th</sup> percentile, which is supported by longitudinal evidence on churning. Data from _Susenas_ panel 2008-2010 show that around 45 percent of households that are poor in 2010 were also poor in 2008 while around 50 percent of the poor in 2009 are not poor in 2010.

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Cost-seeking FDI ( _motive_cost_ ) is negatively correlated with the share of local workers (column 2) as well as the probability of offering supplier assistance (column 4) if this motive has a moderate importance for multinationals.

Resource-seeking FDI ( _motive_res_ ) clearly shows a negative correlation with the share of sales going to the host country if this motive is important (column 3). Moreover, it is also negatively associated with supplier assistance, regardless of the importance of this motive (column 4).

# **4 Which Absorptive Capacities Facilitate FDI Linkages?**

This section focuses on the role of domestic supplier characteristics for FDI linkages. In section 4.1, we present the data, while section 4.2 introduces the empirical model where we relate absorptive capacities with FDI linkages. Section 4.3 examines if there are differences in the extent of FDI linkages between different groups of suppliers, depending on their absorptive capacities. Section 4.4 describes the regression results.

## **4.1 Data**

The focus of sections 4 and 5 is on national suppliers (see section 3.1 for a description of our dataset). The national suppliers’ surveys cover 148 firms in Chile (18), Ghana (26), Kenya (29), Mozambique (36) and Vietnam (39). More than half of the suppliers (88) supply to multinationals in agribusiness, followed by mining (48) and apparel (12). These suppliers produce a variety of inputs across the value chain, as shown in Table 7, ranging from chemicals, to equipment, to food and food processing, to business, technical, and other services, among others.

**Table 7: Distribution of Suppliers by Sector**

|**Sector**|**No. of firms**|**%**|
|---|---|---|
|Apparel accessories|4|2.7%|
|Chemicals|22|14.9%|
|Equipment|22|14.9%|
|Food and food processing|24|16.2%|
|Inputs to mining|8|5.4%|
|Packaging|10|6.8%|
|Seeds|11|7.4%|
|Business services|17|11.5%|
|Technical services|20|13.5%|
|Other services|10|6.8%|
|_All sectors_|_148_|100.0%|

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local VHF database. Each observation in our data represents one of these CIFs. Data from the districts were periodically transmitted to the National Ebola Response Center.

The VHF database includes four different types of cases. Two classifications result from testing: **negative** cases where Ebola has been ruled out; and **confirmed** cases per lab results. In total, the VHF contains data on 8358 confirmed cases. The average patient (reported in Fang et al. (2016)) was 30 years old; and over 70% were above the age of 18. There are two residual categories that are never confirmed with lab tests: **suspected** cases display Ebola symptoms and/or have had contact with potentially infected individuals or animals;<sup>17</sup> and **probable** cases meet the criteria for a suspected case and were either screened by a clinician or died and have an epidemiological link to a confirmed case. Given our interest in reporting, our primary outcome is total cases — the sum across these four case types.

We geocode cases using information on individuals’ residences included in the VHF database (typically, district, chiefdom, and village or parish). The full geocoding protocol is described in Section E.22. While this geocoding process introduces measurement error, we expect this to be uncorrelated with our randomized treatments and, if anything, result in a loss of efficiency. Consistent with this claim, we test whether treated sections have more or longer placenames, or placenames that are more likely to contain spaces (i.e., two word names), and find no substantial or significant differences (see Table E.27). To check the accuracy of our geocoding protocol, we look at the average number of confirmed cases in sections that hosted major Ebola-specific treatment facilities: Ebola Treatment Units (ETUs), Ebola Holding Centers (EHCs), or Community Care Centers (CCCs). We find that sections with ETUs, the largest facilities, reported 484 cases on average; sections without any of the three facilities averaged just 25.2 total cases (see Table E.1).

Our main dependent variable is the count of total cases aggregated to the section-week. We use the date when a case is first entered in the VHF database to determine the week. To demonstrate robustness, we employ a number of alternative specifications, using the inverse hyperbolic sine transformation of the count and the logged count, as well as estimating linear probability and Poisson models (see Tables 3 and E.8).

> 17 Suspected cases include (1) the onset of high fever and contact with a suspected, probable, or confirmed individual or a dead or sick animal; (2) the onset of high fever and at least three of the following symptoms: headaches, vomiting, anorexia/loss of appetite, diarrhea, lethargy, stomach pain, aching muscles or joints, difficulty swallowing, breathing difficulties, or hiccup; any person with inexplicable bleeding; or any sudden, inexplicable death. Suspected and probable cases may have died prior to a lab sample being collected; alternatively, administrative issues may have led to tests being missed or not entered into the VHF.

15
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