rafmacalaba/datause-encoder-data huggingface dataset:
specifications, as well as apply a number of robustness checks to estimation results. While experimental design studies can provide the benchmark results for the impact of specific interventions, our paper offers a couple of advantages. One advantage is that we use nationally representative survey data for a large sample size from around the country.<sup>35</sup> Another advantage is that while a number of experimental studies are designed to vary certain features of the school system one at a time (for example, providing either more textbooks or additional contract teachers), we are able to examine the overall impact of all relevant components. See, for example, Ravallion (2009) for a thoughtful discussion of these issues. However, a combination of a study using nationally representative data and evaluations of smaller-scale experiments may perhaps offer the best of both worlds.

Finally, we do not have data on student performance such as test scores and thus cannot investigate the impact of incentives and teacher effort on student achievement, the ultimate variable of interest. Here we rely on the insights from previous studies. Hanushek and Rivkin (2010) find that teacher quality (as measured by a teacher fixed-effects component) increases student reading and math achievement by between 0.11 and 0.15 standard deviations in the United States. A study that is closer to ours finds that a 5-percent increase in the teacher’s absence rate reduces student learning by 4 to 8 percent of average gains over the year in Zambia (Das et al., 2007).

Our results reveal that teachers engage in strategic choices about effort. Some incentives lead teachers to provide more (observable) after-school tutoring but fewer (unobservable) after-school work hours spent in preparing for classes, and some incentives lead to the opposite choices. To avoid inducing strategic choices that reduce overall effort and lower learning gains, understanding how different forms of pecuniary and non-pecuniary incentives affect teacher

> 35 See, for example, Bold et al. (2012) for a discussion on the difficulties of scaling up a randomization study.

29
# Appendix 2: Parallel trends

The difference-in-difference approach relies on the assumption that in the absence of the PBF intervention, changes over time in the PBF and control districts would be similar. We used the Tajikistan Demographic and Health Survey (DHS) 2012 to test whether the parallel trends assumption could be rejected for the years prior to the launch of the PBF pilot. For the years 2008-2012, we constructed annual indicators for timely antenatal care, receiving at least four antenatal consultations and for vaccination coverage of children.

The results presented in the table below are from a difference-in-difference specification in which we define the period 2010-2012 to be a ‘post intervention’ period. As can be seen, for none of the indicators were we able to reject the parallel trends assumption. We clustered standard errors at the sampling cluster level, which provides a more conservative test in comparison to clustering at the district level as we do in our analysis. The results are robust to changing the pre- and post-intervention periods.

|||Diff-in-diff co<br>|efficient<br>|
|---|---|---|---|
|SelectedIndicators|N|β|SE|
|ANC Visits within 12 weeks|1163|-0.05|0.07|
|4 or more ANC visits|1463|-0.05|0.04|
|BCG vaccination date|2532|0.02|0.06|
|DPT 1 vaccination|2532|-0.01|0.06|
|Polio 1 vaccination|2532|0.01|0.08|
|DPT 2 vaccination|2532|-0.03|0.08|
|Polio 2 vaccination|2532|-0.02|0.06|
|DPT 3 vaccination|2532|-0.02|0.05|
|Polio 3 vaccination|2532|-0.01|0.05|
|Measles vaccination|2532|-0.03|0.06|
|Polio 0 vaccination|2532|-0.04|0.07|

Several caveats, however, should be considered. First, we still rely on the assumption that the parallel trends would have persisted during the years of project implementation. Second, we can only perform these tests for a small set of outcomes of interest. Third, to preserve the anonymity of respondents, the location of DHS clusters is randomly displaced up to 2 km in urban areas and 5 km in rural areas, with 1% of clusters displaced up to 10km. Some clusters may be 36
- 12 -

depend on the type of auction, the characteristics of the auctioned object, and firm and industry characteristics (Branmman et al, 1987). Some auction models have clear predictions for the relationship between winning bids and the number of bidders. It may be less predictable for other types of auctions, particularly under risk-aversion, correlated values and uncertainty concerning the value of the auctioned object

# 3. DATA AND _EMPICAL_ MEHODOLOGY.

There has been very little empirical work on foreign exchange auctions in Sub-Saharan Africa. Apart from policy-based surveys (e.g. Krumm, 1985; Quirck et al, 1987; Roberts, 1989), only the Zambian auctions appear to have been studied in any detail (e.g. Tenorio, 1993; Bates and Collier, 1993; Aron and Elbadawi, 1992). To the best of our knowledge, the only micro-economic research on the SSA auctions motivated by auction theory is due to Tenorio (1993), who tested for the revenue-equivalence of the two types of auctiont which appeared consecutively in the eighteen month Zambian experiment. In general, there have been no controlled experiments on foreign exchange auctions using generated data, nor have the dynamic feaures of repeated auctions been studied.

Yet, there is enormous scope for research on foreign exchange auctions in SSA, both in comparative time-series and cross-sectional panel data studies. The SSA case-studies present a wide spectrum of auction designs and outcomes for cross-country comparisons. In a number of countries, different auction types follow consecutively, allowing within-country comparisons of auction design. For a few countries the data set includes detailed individual bidder data for each auction; this allows an analysis of allocation, of dynamic features such as learning and strategic behavior across auctions, and the determination of the distribution of actual bidder values. Finally, weekly parallel data is available for most of the countries, so that the progress of unification can be followed throughout the transitional auction phase.

A description of our data set is contained in Aron and Elbadawi (1994). The paper discusses design characteristics for the Zambian, Ugandan, Ghanaian and Nigerian auctions, which are summarized in its Table 1. In Table 2 of that paper, basic statistics are given for the auction data, according to auction regimes, and ihese statistics, as well as a number of measures of nor-normality of the data (skewness and kurtosis), are discussed in detail.

## 3.1t Cointegation Modelling in Repeated, Sequential Auctions

The analysis of the individual time series properties of the auction markets' pivotal variables, such as the level and variance of the selling price (exchange rate), the black market premium, and the demand/supply of foreign exchange, shows that the time series structures of these high frequency
# **3.3** Regression Analysis

The method of ordinary least squares is used to estimate<sup>the followingequation:</sup>

**_GGRPCGDP,(.. 4_** _=_ aIDI **+ a2+** **_a 3D 3_** 4C **+** **_a,D +_** _a 6(G1TE),_ (12) **+ a** **_7BMPO + aSHOCKt +_ pu**

where the variables are: (i) GRPCGDPj,0+1.,+: Five year forward moving average of per capita real **GDP** for country (ii) **Dj :** Continental dummy variables; **j = 1,** 2, **3,** 4,<sup>and</sup><sup>**_5_**correspondtoEastAsia, South</sup> Asia, Sub Saharan Africa, Latin America, and Europe,<sup>Middle EastandNorth Africa</sup> respectively; (iii) **(G/TE),, : A** vector of public expenditure ratios for country i:

- **NCURETE =** current net of interest/total expenditure

- **CAPETE** = capital/total expenditure

- DEFTE = defense/total expenditure

- HLTHTE **=** health/total expenditure

- **EDTE** = education/total expenditure

- **TACTE** = transportation and communication/total expenditure

(iv) BMPi,, **:** Premium in the parallel market for foreign exchange<sup>incountry</sup><sup>**_i;_**calculatedas</sup> <!-- Start of picture text --> BMP BMERJ - OER)O 100 (13)<br>OERJ<br><!-- End of picture text --> where BMERI,, **=** Black market exchange rate; and OER., **=** Official<sup>exchangerate</sup>

**13**
# **Table A.20. Predicted poverty rates (and SEs) based on LASSO, Elastic net and Random Forest from NPS 2020/21 to TA 3 using 2020/21 Poverty Line, Tanzania (percentage)**

|||||**TA**<br>|**3**<br>||||
|---|---|---|---|---|---|---|---|---|
|**Method**|**Model M1**|**Model M2**|**Model M3.1**|<sup>**Model**</sup><br>**M3.2**|**Model M4.1**|<sup>**Model**</sup><br>**M4.2**|**Model M8**|**Model M9**|
|1) Multile imutation (PMM)|**18.3**|**18.7**|33.3|**17.0**|41.1|**17.7**|**19.3**<sup>**a**</sup>|**19.6**<sup>**a**</sup>|
|p p|(2.0)|(2.0)|(2.0)|(1.6)|(2.4)|(1.9)|(2.2)|(2.0)|
|2 Mlil ii li|**18.1**|**18.6**|31.8|**17.0**|46.6|**18.5**|**19.4**<sup>**a**</sup>|**19.8**<sup>**a**</sup>|
|) utpe mputaton (near)|(2.1)|(1.8)|(2.0)|(1.6)|(2.3)|(1.9)|(1.9)|(2.0)|
|3 L|8.9|14.3|39.4|16.4|48.4|17.1|15.9|14.6|
|) asso|(2.4)|(2.5)|(2.5)|(2.0)|(3.0)|(2.6)|(2.6)|(2.5)|
|4 Elti Nt|8.9|14.5|39.4|16.4|48.3|11.2|16.2|14.6|
|) asc e|(2.4)|(2.6)|(2.5)|(2.0)|(3.0)|(1.9)|(2.6)|(2.5)|
|5 Rd Ft|13.4|9.7|37.0|16.4|42.8|14.4|10.1|13.3|
|) anom ores|(2.0)|(1.9)|(2.3)|(1.9)|(3.0)|(2.1)|(1.8)|(2.0)|
|_Control variables_|||||||||
|Food expenditures|||Y|Y|||||
|Non-food expenditures|||||Y|Y|||
|Utilities: water, kerosene, lighting|||||||Y|Y|
|Household assets & house characteristics||Y|Y|Y|Y|Y|Y||
|Demographics & employment|Y|Y|Y|Y|Y|Y|Y|Y|
|N1(base survey)|4,644|4,644|4,644|4,644|4,644|4,644|4,644|4,644|
|N2(target survey)|698|698|698|698|698|698|698|698|
|**True poverty rate in TA 1**<br> <br>Note: One-standard-error rule was used to sele<br>standard error of the true poverty rate. Lasso, E<br>subsets: 50% used for training and 50% used f<br>method. 50 simulations are implemented. True|ct lambda. Esti<br>lastic net linea<br>or testing (valid<br>poverty rate is t|mates shown in<br>r models and<br>ation). For mu<br>he estimate dir|boldface or wit<br>Random Forest m<br>ltiple imputation,<br>ectly obtained fro|21<br>(2.<br>h a “<sup>**a**</sup>” res<br>odels are<br>we use fi<br>m the sur|.0<br>2)<br>pectively fall wi<br>trained in the fi<br>ve nearest neigh<br>vey data.|thin the 9<br>rst round<br>bors with|5% confidence<br>when the data i<br>the predictive|interval or one<br>s split into two<br>mean matching|

Note: One-standard-error rule was used to select lambda. Estimates shown in boldface or with a “<sup>**a**</sup> ” respectively fall within the 95% confidence interval or one standard error of the true poverty rate. Lasso, Elastic net linear models and Random Forest models are trained in the first round when the data is split into two subsets: 50% used for training and 50% used for testing (validation). For multiple imputation, we use five nearest neighbors with the predictive mean matching method. 50 simulations are implemented. True poverty rate is the estimate directly obtained from the survey data.

64
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35
# **7. Conclusions**

Credit guarantee schemes have become the instrument of choice for policy makers to increase access to lending, especially for constrained groups such as small or new enterprises. Little has been known, however, about how these schemes vary across countries. This paper is a first effort to fill this gap. Using a survey of partial credit guarantee schemes across 46 developed and developing countries, it provides a first overview of how schemes differ in their characteristics.

We find a large variation in the organizational structure, the role of the government and private sector, and the risk management and pricing mechanisms that partial credit guarantee schemes use around the world. However, there is surprisingly little systematic variation in many of these characteristics with economic and financial development.

Our survey shows an important role of government in partial credit guarantee schemes around the world, but mostly limited to funding and management, and much less in credit risk assessment and recovery. This might be for the better, as we also find that where government is involved in credit risk assessment, default rates are typically higher. Older schemes are also more likely to be government funded and managed and also have higher loan losses, consistent with the notion that the costs and liabilities of a PCG fund become obvious only after some time. We find a surprisingly low incidence of risk-based pricing and limited use of risk management mechanisms. However, there are some indications that funds that take on more risk also compensate for this by better risk management.

While this database is an important first step to better understand the typology of credit guarantee schemes around the world, there are also clear limitations. Using crosscountry data such as the ones presented here do not allow to properly asses the effect of different characteristics of partial credit guarantee schemes on banks’ risk-taking decisions and on the effect that credit guarantee schemes have on access to credit, entrepreneurship and job creation. Such assessments would require loan-level data, 24
_Table 3: The estimated farm size-productivity relationship_

|||||**Extended m**<br>|**odel**<br>||
|---|---|---|---|---|---|---|
||**Basic**|**No SoilQuality**|**Full Model**|**2000**|**2004**|**2008**|
|**Frontier**|‐0.046|‐0.062**|‐0.050*|‐0.071**|‐0.072**|0.023|
|**Efficiency**|‐|‐0.054***|‐0.048**|‐0.051**|‐0.051**|‐0.055**|
|**Combined**|‐0.046|‐0.116***|‐0.098**|‐0.122**|‐0.123**|‐0.032**|

_Source_ : Authors’ estimates using the 62-village panel survey. _Note_ : *, **, and *** indicate statistical significance at 10, 5, and 1 percent level.

Two notable findings emerge from these results. One is that the basic model, by ignoring the inefficiency specification, is likely miss-specified and the farm-size productivity relationship inaccurately estimated. This miss-specification is also indicated by the much higher value of lambda for the basic model (see model statistics at the bottom of Annex Table A.3) than the other models, indicating that the inefficiency variance is significantly higher than the random variation (indicative of miss-specification). The second finding is from the extended model, which suggests that the IR, although still statistically significant, appears to have diminished over time, with the scale elasticity much smaller in 2008 compared to previous years.

The third important set of results from the SPF estimation relates to the growth in TFP and its constituent components. Using the extended model coefficients, in addition to the scale elasticity, the results highlight two important findings: (i) there is no technical change detected between 2000 and 2004 (the coefficient on the 2004 year dummy is essentially zero), but this changes dramatically by 2008, with a large, positive and statistically significant parameter value on the 2008 dummy. As noted earlier, 2004 was a bad year weather-wise, and the year dummy is likely picking up a combination of the negative weather shock and technical change, and likely unable to distinguish between them. The estimate for 2008 on the other hand shows a very large 33% improvement over 2000. (ii) Technical change is positively correlated with farm size (the interaction between year dummy of 2008 and farm size is statistically significant and positive) – meaning that larger farmers benefited relatively more from technical change over this period.

The association of the pace of technical change with farm size is an important finding and warrants careful interpretation. It is tempting to conclude, as is traditionally assumed, that perhaps with better access to technology or fewer constraints to adoption, larger farmers benefit more or earlier. The data, however, present a different story – it is the smaller farmers who appear to have been 19
question each was randomized to a single hypothetical reward amount (Tsh 10,000 / 20,000 / 50,000 / 100,000) and asked how much that amount would motivate behavior change. Table 4 reports again a consistent dose-response relationship, with higher amounts related to higher self-reported behavioral change motivation. Interestingly, those actually enrolled in the reward arms reported higher levels of motivation than did the control respondents when reporting about the hypothetical reward scenario.

These motivation questions were repeated again at the 12-month intervention endpoint, as reported in the middle panel of Table 4 (the questions were not asked prior to the 8-month survey). The above dose-response patterns were replicated. A further finding is that reported motivation levels are uniformly higher at 12-months than they were at 8-months, suggesting that there may have been further learning and behavior change by participants during this interval, which is an argument for repeated rounds of incentivized behavior over an extended period of time. By this endpoint, 79% of the high-value arm enrollees reported ―very much‖ motivation, with only 5% reporting no motivation.

Finally, the bottom panel of Table 4 reports on parallel questions that were asked at 12-months in regard to the lottery incentives. We first note that 89% of high-value arm respondents reported ―very much‖ motivation from the lottery, which is even higher than for the cash rewards. This is despite the fact that the respondents had already participated in two rounds of the lottery, after which they should have been aware that the odds of winning the actual 100,000 lottery were approximately 1%, thus the expected value of the lottery was far lower than the certain cash rewards. Second, we note that the responses by control individuals (asked to imagine a single hypothetical lottery amount in which eligibility was conditioned on negative STI results) were quite similar to those of the actual high-value and low-value arm respondents; perhaps the fact that the control arm enrollees had already been actually eligible for the lotteries (but regardless of STI status) had made them better informed about how the lottery could affect their motivation. Third, it is evident from Table 4 that there is not a dose-response relationship between the different hypothetical lottery amounts and the degree of projected behavior change motivation. This is despite the fact that these control respondents had all been ―anchored‖ by the actual lottery amount of Tsh 100,000, and thus might be particularly 22