rafmacalaba/datause-encoder-data huggingface dataset:
The setup of this paper is as follows. In section 2 we present the design of the RCT we implemented in Burkina Faso. Section 3 presents the results, and section 4 provides insight into the mechanisms why the threshold group payment scheme performed worse than the linear group payment scheme. Section 5 presents the results of the laboratory experiment, and section 6 concludes.

# **2 Design of the randomized controlled trial**

## **2.1 Intervention description and conceptual framework**

Our project started in July/August 2017 with planting about 33,500 young trees on 66 well-defined degraded forest lands across 11 protected forests – on average about 500 trees per reforestation plot. The trees on each of these plots were to be maintained by groups of five individuals recruited for the project from nearby communities. Each management group would receive money depending on the number of newly planted trees still alive on their plot at the beginning of the next rainy season, nine months later. Each individual group member would receive an equal share of the group payment, independent of the amount of effort they themselves invested in tree maintenance.

Two different payment schemes were implemented. The linear group payment scheme consisted of paying maintenance groups 300 FCFA (about 53 US cents<sup>4</sup> ) for each tree that is still alive at endline. The amount of money received by management groups in the threshold group payment scheme depended on the highest threshold level met by the number of trees still alive, at endline, on their plot. Thresholds were set at 400, 300, 200 and 100 living trees. The group payment was 135,000 FCFA (about US $ 239) if 400 or more trees were still alive at the beginning of the next rainy season, and it fell by 30,000 FCFA (or about 53 dollars) with every threshold that was crossed. Figure 1 provides a graphical representation of the two incentive schemes. Because parameters were chosen such that group payments are the same in the two treatment groups for survival rates in the middle of each threshold level, the two treatments are ex-ante payoff equivalent; see Appendix A for a formal proof.

> World Bank (2018).

> 4At endline the official exchange rate was $1.77 for 1,000 FCFA.

7
(i.e. students, retirees and homemakers; the unemployed are included). Morality is dichotomous, and ability is measured by a 7-point ordinal scale, so we compute Spearman’s rather than Pearson’s correlation coefficients.

The morality and ability indicators are both included in one or more surveys from the 3<sup>rd</sup> , 4<sup>th</sup> and 5<sup>th</sup> waves of the WVS in 74 countries.<sup>12</sup> For each of these three waves, the Data Appendix shows which of these 74 countries participated and the year in which the survey was conducted. There are 38 countries that participated in only one of the three waves. In 24 countries, surveys were conducted in two waves, and the other 12 participated in all three waves. With 122 total surveys in the 74 countries, the mean number per country is 1.75. The mean survey year is 2002.

Following Bjornskov (forthcoming) and others, we take the mean values of WVS variables for the 36 countries with multiple surveys, based on the premise that the within-country variation over time is small and measured with substantial error relative to the cross-country variation in the surveys. As Bjornskov (forthcoming) finds for interpersonal trust, morality and ability (and their correlations) appear to be fairly stable over time.

Summary statistics of our data are presented in Table 1. The mean level of morality is 21%, ranging from a low of 5% for Uganda to a high of 49% for Sweden. In general, developed countries rank higher on morality, but the value for Uganda’s equally-poor neighbor Tanzania is 29%, and the Dominican Republic’s 39% places it above the majority of developed countries.

For most countries, there is a positive but modest correlation between morality and ability. The correlation is negative but small in Uganda (-.04), Mali (-.10) and Tanzania (-.13). The mean correlation for the 74 countries is +.14, with a maximum of +.27 (for Czech Republic).

> 12 The morality question was not included in the first two WVS waves (1981-84 and 1990-93). We drop several countries (including Andorra and Cyprus) with WVS data on ability and morality due to missing data on income, trade or other key variables in the analysis. Colombia is dropped because its survey included an additional response category for the morality indicator, so its value is not comparable to those of other countries.

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Several studies have examined empirically the likely effects of different preference schemes (see Hoekman and Özden (2005) for a survey of the literature). The empirical literature on preference schemes highlights several difficulties limiting the benefits available for the recipient countries. Some papers pointed out that administrative requirements and technical requirements (such as rules of origin) of preferential programs often impose considerable burden on traders, especially on lesser-developed countries, resulting in low utilization rates of the preferences.<sup>3</sup> Several preference schemes, such as the GSP preferences of the US, are limited to some sectors, in which developing countries lack comparative advantage<sup>4</sup> (only 53 per cent of dutiable imports from developing countries are eligible for preferences under the US's GSP<sup>5</sup> ). Trade expansion effects of certain preference schemes are further limited by quantity (quota) ceilings, product exclusions and other non-tariff trade policy instruments limiting market access.<sup>6</sup> When the preference schemes include export ceilings these are often binding.<sup>7</sup> Özden and Reinhardt (2004) find that countries dropped from the US's GSP scheme subsequently adopt lower trade barriers than those remaining eligible. The authors conclude that full integration into the reciprocity-based world trade regime rather than continued GSP-style preferences would be more beneficial for developing countries.

The current paper explicitly examines the non-least developed ACP countries’ preferential trade with the EU. Our objective is to explain the determinants of preferential exports of non-least developed ACP countries towards the EU and to assess the impact of preferences on trade volumes. To the best of our knowledge, the impact of the EU’s preference scheme has not been analyzed using a measure of preferential and non-preferential tariffs in previous empirical studies. The paper also investigates whether there exists a threshold in the offered duty reduction under which traders have no incentive to ask for preferences since the costs of obtaining these exceeds their benefits. As far as we are aware, the idea of a threshold value in the magnitude of the preference margin (the difference between preferential and third country tariffs) has not yet been empirically analyzed. This is the main contribution of this paper.

> 3 UNCTAD (1999, 2000), Brenton and Manchin (2003), Falvey and Reed (2002), Krishna and Krueger (1995), Cadot,  et al. (2003), Candau, Fontagne and Jean (2004)

> 4 Devault (1996).

> 5 The information here comes from UNCTAD (2001).

> 6 Baldwin and Murray (1977), Sapir and Lundberg (1984), Clark and Zarilli (1992)

> 7 MacPhee and Rosenbaum (1989), Hoekman and Kostecki (2001).

4
the growing interest in understanding the distributional aspects of property tax compliance by gender.

**Fact #3: Women face slightly higher effective tax rates than men, driven by ownership of lower-value properties and a** **_de jure_ regressive tax schedule.** Our dataset allows us to calculate the statutory ETR (tax owed as a fraction of property assessed value) and the empirical ETR (tax paid as a fraction of property assessed value). Three key insights emerge. First, as shown in Figure 6, taxpayers at the lower end of the property value distribution face ETRs that are 2 to 3 times higher than those at the top, regardless of gender. This disparity arises from fixed charges of the tax schedule that disproportionately burden low-value properties. Second, due to high non-compliance, the empirical ETR is substantially lower than the statutory ETR across the distribution. While the schedule is _de jure_ regressive, it becomes more proportional _de facto_ when accounting for non-compliance. Third, as illustrated in Figure 7, women face slightly higher average effective tax rates (both statutory and empirical) compared to men and co-owners. This difference is driven by women’s greater ownership of lower-value properties (Figure 3) and the mildly regressive nature of the tax schedule. Overall, these findings suggest that non-compliance and ownership patterns may undermine both vertical equity (tax disparities across the distribution) and horizontal equity (tax burden across gender).

**Fact #4: Women are slightly less likely to use electronic methods to pay property taxes.** Table 3 shows differences in means from linear probability models using various payment methods as dependent variables. The first two columns document that, on average, women are about 2 percentage points more likely to pay all their property tax bills in cash (compared to a baseline of 60% who use cash). Conversely, they are less likely to use online payment methods. The result remains similar when we consider the fraction of tax payments made online, as shown in the last columns. These results hold whether we perform a simple comparison of means (odd columns) or include controls for assessed value, age, and geographical location (even columns), suggesting relatively small differences in payment method preferences between men and women.

# **5.2 A Randomized Tax Communication Campaign**

Do men and women respond differently to tax enforcement measures? Tax administrations increasingly use communication tools such as letters, emails, and text messages to enhance tax compliance and streamline their collection strategies. We examine whether men and women exhibit different responses to such interventions. While the effect of taxpayer reminder letters on tax compliance and collection is well documented in existing, rigorous RCTs (Antinyan and Asatryan, 2024; Hjort, Moreira, Rao, and Santini, 2021; Mascagni, 2018), studies specifically ad10
dates, for _Bolsa Familia_ , and in Uruguay, where voters do not reward parliament or local councils, just the President and the incumbent government. A different dimension of heterogeneity is highlighted by Larreguy, Marshall and Trucco (2015), who find that central government leaders gained in popularity from a land titling program, but local leaders lost support, since it undermined clientelist strategies. Partisan differences are also important to the theoretical framework of Imai, King and Velasco Rivera (2016), who argue that in cases where programs are supported by both (or all) relevant parties, such as Mexico’s Seguro Popular health reform and Progresa CCT program, there is no logical reason why voters would reward specific politicians (i.e. incumbents) rather than out-of-power parties who also support the program.

In Tanzania, the ruling party, CCM, has held power at the central level continuously since independence, and the vast majority of local (village-level) governments are also controlled by CCM. The ITN distribution was predominantly an initiative of the central government and international donors (although local leaders participated in implementation), so if voters are “correctly” attributing credit where it is due, there should be a reduced treatment effect in opposition controlled localities, since the opposition had no power in the central government or the Ministry of Health, and an increased treatment effect in CCM-controlled settings.

The National Panel Survey collected information on local political leaders, such as their bureaucratic or elected post and their partisan affiliation. This enables an examination of the interaction of treatment with villages where a) all recorded village level officials are from the ruling party (this represents 43% of villages), and b) villages where more than 50 percent of village officials listed on the community leader roster are from opposition parties (14% of villages). For these models, attention is restricted to village level leaders, since information about the partisan composition of higher levels of the political system (i.e. ward councils) is not available in the dataset. There is no evidence that citizens boost approval of CCM officials more than opposition, and similarly no evidence that they credit opposition leaders any less, even though the opposition had no clear responsibility for the program at higher policy levels (Table A6).

22
as difficulties faced by refugees in engaging with available educational opportunities, their and 3% as non-family legal guardians. Caregivers who fled the situation in Ukraine come from all Given the sampling design and the limited number of observations in the final sample, the survey is not cannot be extrapolated beyond the respondents. However, the number of observations in the final sample the Joint IDP Profiling Service (JIPS, 2020) (0.9%)), although the number of observations is remarkably lower.
distributions of consumption and income from 1981 to 2017 that closely align with the World Bank’s official estimates.<sup>10</sup> For comparisons of growth as estimated by national accounts and surveys, there is the additional concern that heterogeneity in the survey data over time can potentially create noisy growth estimates. To partially address this concern, consumption and income surveys are considered separate series for each country, so that we do not calculate growth rates from an income survey in one year and a consumption survey in another. But there remain many ways in which growth estimates of consumption surveys (or income surveys) can be problematic due to changes in survey methods and practices. Jolliffe (2001), Beegle et al. (2012), Jolliffe et al., (2014) all document how changing instrument design over time within a country can change measured consumption, which will appear as growth (or contraction) over time independent of whether national well-being has in fact changed. As survey methods and questionnaires change over time within a country, PovcalNet typically does not post-adjust data from previous years for that country. Metadata on survey comparability suggests revisions in survey methods are widespread and create a break in comparability for two-thirds of the 164 countries that have data over time.<sup>11</sup> As further evidence of this problem, the World Bank is only able to produce comparable data for mean household survey growth required for the shared prosperity measure (requiring comparable data over a five-year period) for 88 of the 168 economies in its database.<sup>12</sup> For the assessment of growth rates, where comparability in the measures matters significantly, we create an ancillary analysis file based on the World Bank’s _Global Database of Shared Prosperity_ . This database is designed with the objective of assessing growth as measured 10 Following an approach similar to that taken by Lakner et al. (2019), we use the ungroup command included in the DASP Stata Package (Abdelkrim and Duclos, 2007) to generate a national distribution of 10,000 points for each reference year, based on Lorenz curves from PovcalNet. The resulting estimates of poverty and inequality are within 1 percentage point of direct PovcalNet estimates based on microdata in more than 95 percent of the cases.

11 Criteria and data on survey estimate comparability are described in Atamanov et al. (2019). The comparability metadata is available in the World Bank’s GitHub Repository for PovcalNet: <u>https://raw.githubusercontent.com/worldbank/povcalnet/master/metadata/povcalnet_metadata.csv</u> 12 Global Database of Shared Prosperity and Median Income/Consumption, circa 2013-2018, as of March 20, 2021: <u>https://www.worldbank.org/en/topic/poverty/brief/global-database-of-shared-prosperity.</u> A limitation of household surveys is that they are conducted with uneven frequency and with low consistency in methodology and implementation over time. Many countries lack surveys for at least five years or longer (Serajuddin et al., 2015).

8
Now, to what extent do we observe persistence in access to opportunities in the LAC region? To estimate persistence, we measure the correlation in the rankings among subgroups within countries during the period of analysis, using the Spearman’s rank-order correlation.<sup>7</sup> In particular, we measure both the ranking correlation among consecutive censuses and the correlation with respect to the ranking in a year (or census) of reference. In the former case, given the irreversibility of fixed investments required to expand coverage of basic public services, we would expect that access to electricity, water and sewerage showed higher persistence in time. In the latter case, we expect the persistence to dissipate as we move farther away from the reference year.

In practice, we observe that the ranking correlation in consecutive censuses is relatively high (above 0.90 on average) for electricity, water and sewerage, both in countries with high and low geographic heterogeneity (e.g., Peru and Uruguay, respectively) and for different coverage rates (e.g. high coverage countries such as Costa Rica and low coverage like Bolivia). However, once countries are closer to achieving universal coverage of a basic service (such as electricity in Uruguay after the mid-1990s), the ranking becomes more sensitive to changes in time. A potential explanation is that, once a country approaches universal coverage, access rates for all subgroups 7 The Spearman correlation calculates the Pearson correlation for variables that are converted to ranks. Broadly speaking, a positive correlation coefficient indicates a positive relationship between the two variables, while a negative correlation coefficients expresses a negative relationship; a correlation coefficient of 0 indicates that no relationship between the variables exists at all.

14
12 (b) Questions should be simplificd by breaking thcm down into thcir smallest components so that it is easicr for respondcnts to makc accurate cstimatcs.

(c) The: questionnaire shou!d be designed so that it is easy for the interviewer to fill in, e.g. bJy using large white spaces, boxes, arrows, clcar instructions and a good reference manual.

(d) The length of the questionnaire will affect the time of the interview. Depending on the culture, interviews longer than two hours per household can reduce the quality of the responses.

(e) Control questions should be included for important variables so that the accuracy of responses can be cross-checked.

ON' The appropriate language and local units of measurement should be incorporated in the questionaalre for each d;ferent area that is to be surveyed.

(g) Respondents should be asked a general concluding question where they have an opportunity to give their comments and views on topics that they think are of relevance to the survey. This can generate useful information and give the respondent an opportunity to participate in questionnaire design by answering his/her own question.

These are all elements of a good questinnnaire. Some of the key items that can be covered in a household energy survey are presented in Annex 2. Care should be taken in duplicating the wording and format used in these examples as they were not designed for specific cnuntries or regions and may not be applicable or relevant to your situation.

Some Common Mistakes. The following is a list of errors which are frequently made in the preparation of household energy survey questions. The list is not comprehensive but one should certainly avoid: (a) asking questions that are not relevant to the issues being addressed in the survey. In many instances. highly specialized questions cannot be answered by the majority of the population. In addition, there is always the temptation to insert many superfluous questions; (b) concentrating on obtaining too much factual information, while forgetting that, in the end, the data must be analyzed. This Information gathering overkill can lead to needlessly long interviews, which affects the quality of the data collected; (c) asking double-barreled questions. These involve asking for two or more pieces of information in the same question. For instance, "do you use electricity or kerosene for lighting?" is really two or even three questions and should be separated into its individual parts; (d) failing to use screening techniques so that relevant questions are asked of relevant populations. To ask a person who has never used electricity or kerosene for lighting to compare them is not appropriate; (e) not distinguishing between questions that are used for obtaining information and those that are intended to assess the respondent's opinion on certain issues. The forts for asking information and opinion questions is quite different. Asking a rebpondent how much charcoal he now uses requires a different approach compared to asking an opinion on why charcoal is used;
**Table 8. Drug and laboratory costs for treating HAIs**

|**Country**|**Drugs**<sup>**1**</sup>|**Laboratory**<sup>**1**</sup>|**Total**<sup>**1**</sup>|**High cost scenario**<sup>**2**</sup>|
|---|---|---|---|---|
|Angola|$21.0|$15.1|$36.1|$86.6|
|Congo, Dem.<br>Rep.|$22.8|$16.4|$39.2|$94.1|
|Ethiopia|$12.9|$9.3|$22.2|$53.3|
|Kenya|$17.6|$12.7|$30.2|$72.5|
|Madagascar|$28.5|$20.5|$49.0|$117.6|
|Mozambique|$17.7|$12.8|$30.5|$73.0|
|Sudan|$6.8|$4.9|$11.8|$28.2|
|Tanzania|$18.1|$13.1|$31.2|$74.8|
|Uganda|$15.7|$11.3|$26.9|$64.6|

Sources:<sup>1</sup> Aerts et al (2022) for Mozambique, converted to other countries using PPP.<sup>2</sup> Gidey et al (2023) for Ethiopia in the high cost scenario The estimation of the drug costs of AMR in this study is complicated by the same factors as for HAI (a. through d. above), in addition to (e) whether first line drugs were attempted before switching to second- or third-line drugs; (f) which second and third line drugs are used; and (g) the unit cost of the second and third line drugs. Also, the additional laboratory costs will depend on what laboratory tests are required to successfully diagnose and monitor antimicrobial resistance infections.

In Ghana, Otieku et al (2023) found that an AMR infection (compared to HAI without AMR) increased drug cost by 30% and increased laboratory cost by 42%.

Due to lack of data on these variables to estimate the costs of treating infections with AMR, it is assumed that the costs will be double the costs of treating HAI without AMR.

# 6. Additional length of stay

Manoukian et al (2018) conducted a systematic review and meta-analysis of the impact of healthcare-associated infections on length of stay. They included 36 studies in the quantitative analysis. There is considerable variability in the estimates of excess days due to HAI, with a range of 1.2 to 26.4 days. Studies used a variety of statistical methods, some being more accurate than others. Still the majority of studies use time-fixed method, which risks overestimating the excess length of stay (De Angelis et al, 2010). Based on Manoukian et al (2018), bloodstream infections cause an average excess days due to HAI ranging from 2.7 days for regression technique to 15.9 days for group comparison, while for gastrointestinal infection caused by Clostridium difficile averages range from 2.3 excess days for multistate modeling to 14.4 excess days for regression technique. No overall average is provided by the study across statistical techniques and across infections.

Three studies were found from the nine countries, or neighboring countries. In Ethiopia, Gidey et al (2023) found average length of stay (ALOS) 8.3 days longer among patients with HAI than non-HAI patients (18.85 vs 10.59 days). Also from Ethiopia, Sahiledengle et al (2020) found ALOS was 11.5 days for pediatric admissions with HAI compared to 6.5 days for non-HAI, giving an addition ALOS of 5 days. In Tanzania, the mean postoperative hospital stay was 5.4 days for uninfected patients compared with 13 days for those with surgical site infection 35