rafmacalaba/datause-encoder-data huggingface dataset:
# Figure B.11: Direct effects on pre- and post-intervention bills

<!-- Start of picture text --> Timely payments Timely and past-due<br>only payments<br>(a) Payment rates in levels<br>% paid the bill % paid the bill<br>COVID-19 Intervention COVID-19 Intervention<br>60 60<br>billing periods bill billing periods bill<br>55 55<br>50 50<br>45 45<br>Treated (pooled) Treated (pooled)<br>40 40<br>Pure Control Pure Control<br>35 35<br>30 30<br>25 25<br>20 20<br>2019m1 2019m4 2019m7 2019m10 2020m1 2020m4 2020m7 2020m10 2021m1 2019m1 2019m4 2019m7 2019m10 2020m1 2020m4 2020m7 2020m10 2021m1<br>Billing Period Billing Period<br>(b) Difference relative to pure control group<br>Treatment Treatment<br>effect (p.p.) effect (p.p.)<br>COVID-19 COVID-19<br>6 6<br>billing periods billing periods<br>5 5<br>Oct 2020: Oct 2020:<br>4 4.4 p.p. 4 4.2 p.p.<br>3 3<br>2 2<br>1<br>1<br>0<br>0<br>-1<br>-1<br>2019m1 2019m4 2019m7 2019m10 2020m1 2020m4 2020m7 2020m10 2021m1 2019m1 2019m4 2019m7 2019m10 2020m1 2020m4 2020m7 2020m10 2021m1<br>Billing Period Billing Period<br><!-- End of picture text --> _Notes_ : These figures show the effect of the communication campaign on payment rates of pre- and post-intervention bills. The left panels only consider timely payments, defined as bills paid before the 27th of the corresponding month (i.e., any payment made after the 27th is considered unpaid). Hence, pre-intervention bills mechanically exclude any past-due payment triggered by our intervention. The right panels consider timely as well as past-due payments made until December 2020 and, thus, capture backward payments triggered by our intervention (e.g., individuals who, after receiving the letter, pay the October 2020 bill as well as previous unpaid bills). The top figures show payment rates in levels for treated units (black line) and pure control units (gray line), for 24 consecutive monthly bills between January 2019 and December 2020. Treated units are pooled from groups _Tg_ = 1 _,_ 2 _,_ 3. The bottom figures report total treatment effects—i.e., the difference between treated and pure control units—and 95% confidence intervals for the 24 billing periods. The letters were delivered between September 28th and October 7th. The vertical bar denotes the start of the COVID-19 pandemic in Argentina. Each coefficient is estimated in separate regressions. Standard errors are clustered at the block level. The red line shows no difference on timely payments for pre-intervention bills. In contrast, when we account for past-due payments, the blue line shows that our intervention nudged some individuals to catch up with unpaid bills from April 2020 onwards.

B-22
<!-- Start of picture text --> =o<br>mC<br>=i<br><j<br>aDo f—_]CO<br>=<br>=<br>=<br>5S<br>=<br>=L=7)<br>eSa<br>=<br>2<br>2a<br>s<br>=<br>fo]<br>Ces & = < & <<br>Or fos (os<br>aa Seso <<Lo <<ss <<Oo Sesv<br>Ghana Kenya zambia<br>PI Neo Contract and not known to be on VC (Eon Contract but not known to be on VC<br>Ho Contract but known to be on VCO (NS on contract and known to be on VC<br>Source: Authors' calculations based on survey responses<br><!-- End of picture text --> <!-- Start of picture text --> =s<br>s=<br>a<br>=—Lo a<br>uo<br>—<br>L—>]<br>=<br>bo<br>=<br>mm<br>—<br>a)<br>=o<br>a<br>4<br>2<br>2a<br>s<br>=<br>oa<br>& & & & <& <—<br>Or so Or se ow sx<br>Ghana Kenya Zambia<br>FY Mo Contract and not known to be on VC FY On Contract but not known to be on VC<br>FY No Contract but known to be on WC FY On contract and known to be on VC<br>Source: Authors' calculations based on survey responses<br><!-- End of picture text -->
<!-- Start of picture text --> Figure 4: Observed and simulated labor market status proportions and time usage per spouse and having children<br>Husbands Sample Wives Sample<br>No Children Children No Children Children<br>100%<br>90%<br>80%<br>70%<br>60%<br>50%<br>40%<br>30%<br>20%<br>10%<br>0%<br>NP 56 UE 19 PT 10 FT 15 NP 43 UE 24 PT 12 FT 21 NP 82 UE 10 PT 3 FT 5 NP 83 UE 10 PT 2 FT 4<br>Husbands Simulated Wives Simulated<br>No Children Children No Children Children<br>100%<br>90%<br>80%<br>70%<br>60%<br>50%<br>40%<br>100%<br>30%<br>50%<br>20%<br>0%<br>10%<br>NP 53 UE 16 PT 10 FT 21<br>0%<br>NP 53 UE 16 PT 10 FT 21 NP 41 UE 20 PT 12 FT 27 NP 86 UE 5 PT 3 FT 6 NP 85 UE 5 PT 3 FT 7<br>Leisure Work Home production<br>Source:<br><!-- End of picture text --> _Source:_ Author’s calculations based on 2017 UNDP-WB-EC Roma Regional Survey.

_Note:_ Abbreviations: FT= employed full-time; PT= employed part-time; U= unemployed; NP= nonparticipant. The numbers next to the labor market labels are the proportion of husbands and wives in each labor market state for each country. Per panel, the proportion of husbands and wives should sum up to 100. Because of approximation, for some panels, the sum is equal to 101. Each bar represents the average time allocation between home production, leisure, and work of husbands and wives on each labor market state.

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# **1.  Introduction**

Entrepreneurship is essential for the continued dynamism of the modern market economy and a greater entry rate of new businesses can foster competition and economic growth (Klapper, Laeven and Rajan, 2007; Djankov, La Porta , Lopez de Silanes and Shleifer, 2002). In this regard, a comprehensive longitudinal study of entrepreneurial activity can assess time-varying and time-invariant determinants of firm-creation, and its relationship to economic growth and poverty reduction. Furthermore, from an evolutionary economics perspective, new research suggests that disparities in economic growth between advanced and less developed countries can narrow owing precisely to the growth of entrepreneurial activity (Galor and Michalopoulos, 2006). Empirical data can also help us better understand how entrepreneurs interact within their respective networks, wherein new business ideas are generated and businesses are created (Stuart and Sorenson, 2005). Additionally, there is a strong need to develop data sets to study how economic and political factors affect entrepreneurship. For instance, Brander, Hendricks, Amit, and Whistler (1998) used a longitudinal data set on the evolution of firm formation in Canada to document that economic growth is driven by new entry rather than by the growth of existing firms.

This study offers a methodology for collecting data on new business creation, serving as a first step in enabling research on the dynamic of entrepreneurial activity. Furthermore, the data can be used as a benchmark for changes in the composition of the private sector, and further advance the study of the impact of regulatory, political, macroeconomic, and institutional changes on entrepreneurship and growth.

We find that business entry and density rates are significantly related to country-level indicators of economic development and growth, the quality of the legal and regulatory environment, ease of access to finance, and prevalence of informality. In the multivariate panel analyses, we find that the business environment, specifically the ease of starting a business and political corruption, remain significant indicators of total firm registrations, even after controlling for the level of economic development. These results are thus consistent with prior work on the efficient allocation of inputs and other resources to entrepreneurial activities (Jovanovic, 1982). We also find significantly higher entry rates in countries with better governance. Case studies show the impact of political, institutional, and tax reform on new business creation. These results can guide effective policymaking and deliver new capabilities for identifying the impact of reforms.

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41 Table 3: Labor market outcome variables: descriptive statistics

||Fu|llsample||S|HI = 1|||SHI =0||
|---|---|---|---|---|---|---|---|---|---|
||Mean|SD|Obs|Mean|SD|Obs|Mean|SD|Obs|
|Gross wage|1115.49|876.72|257|1555.22|921.52|119|736.31|626.16|138|
|Unemployment|11.68|5.91|229|11.66|6.16|162|11.73|5.29|67|
|Registered unemployment|9.27|8.26|295|12.98|9.11|141|5.87|5.56|154|
|Empl-to-pop - ILO|51.39|6.31|150|51.22|5.96|110|51.86|7.25|40|
|Empl-to-pop - TransMONEE|67.31|9.00|360|64.54|9.12|158|69.47|8.30|202|
|Informal economy|21.82|21.07|238|22.35|19.94|93|21.49|21.82|145|
|Self-employment|17.24|9.26|190|16.13|8.85|132|19.77|9.73|58|
|Employment in agriculture|25.26|16.64|268|23.07|18.93|162|28.61|11.64|106|

_Note:_ Mean, standard deviation (SD) and number of observations (Obs) for the full sample and for the sub-samples of observations with the SHI dummy equals to one (SHI=1) and zero (SHI=0).
**Table 9: Cellulosic biomass in China**

||Generat<br>Mill|ion Potential<br>ion tonnes|Current Utilization|
|---|---|---|---|
||Current(2008/2009)|2020(estimated)||
|Agriculture residues|650.55<sup>a</sup>(2010)|679.22<sup>b</sup>|15% for burning, 15% for<br>returning to the field, 24% for<br>fodder, 43% for fuel wood, 3%<br>for industry use.|
|Forest residues|854.56<sup>d</sup>(2010)|965.39<sup>b</sup>|Part of bush residues was used<br>to feed, fiber, etc.|

Note: a. data from Chang, et al. 2012

# **3.4.2 Supply cost**

The production cost of 2<sup>nd</sup> generation biofuels is full of uncertainties. Production cost for 2<sup>nd</sup> generation biofuels in the literatures range between USD 0.60/liter and 1.30/liter (4937.4 and 10697.7 Yuan /tonne<sup>4</sup> ) (Ralph, et al, 2010). The pilot scale cost in China is about 7845 Yuan/tonne based on the techno-economic analysis of 300 tonnes project (Table 10). The supply cost is higher than that of gasoline, and lacks of comparative economic advantage. The feedstock cost is relative low, about 19.8% of total production cost. This is partly because the feedstock requirement of 300 tonne demonstration project is not very high. With the increase of production scale to deployment & commercialization stages, the feedstock price will inevitably increase due to long collection radius. Therefore, government subsidies are required.

# **3.4.3 Challenges**

The technology uncertainty is the biggest challenges. Although the Chinese government has put lots of attention on technology R&D of 2<sup>nd</sup> generation biofuels, and it is expected that the 2<sup>nd</sup> generation biofuels will become commercially viable within 7~10 years, it will not play vital role on target achievement by 2020.

# **4. Policies needed to achieve 2020 targets**

# **4.1 Screening of current policies on biofuels deployment relevant policy**

A large number of policies, ranging from command and control instruments (i.e., standards, mandatory and entry regulation) and fiscal and economic measures (tax exemptions and subsidies) have been introduced in China to support the development of biofuels (see Appendix Table A). These policies are aimed at different stages of the biofuels chain can be summarized in Table 11, covering production of feedstock, and conversion of feedstock to biofuels and consumption of biofuels. For fuel ethanol, most of the policies were drafted before 2007 and applied to designated projects only. Since 2007, there are several preferential policies for biodiesel, especially for waste oil-based biodiesel.

> 4 Exchange rate is 6.5 Yuan/ USD; the density here used is 1266 l/tonne

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ROSCAs, and “cash kept at home or in a secret hiding place, that is not for daily living expenses”), and in-kind savings (advance purchase of farm inputs, business inventory, and bags of maize stored for later use). These three categories are mutually exclusive and exhaustive. For ease of comparison to the administrative data, the first column of Table 5 includes only savings in NBS accounts. Columns (2) - (4) are the three categories described above. Column (5) is total liquid savings, the sum of formal and informal savings, and column (6) is total household savings from all sources.

Directly depositing money into NBS accounts increases self-reported savings by MK 1,670 as measured one week after the transfers. The effect is smaller than in the administrative data, perhaps because the control group reports a higher level of savings at NBS than observed in the administrative data, but reflects the same trend: the savings default increases the amount of money in NBS accounts. Because we lack expenditure data after the transfer for the eight day delay group, Panel B has a smaller sample and thus results are not directly comparable to those using administrative data. Nonetheless, the magnitude of the effect of the savings default on NBS balances after two weeks is remarkably consistent with the administrative data.

Columns (2) to (6) show that the increase in money saved at NBS reflects a change in the composition rather than the total value of savings. Focusing on results after one week, where data for the full sample are available, we see that total savings in formal financial instruments rise by an amount comparable to the increase in savings at NBS (column 2), and that the change is more than offset by a decline relative to the cash transfer group in informal savings (column 3), which includes cash kept at home. In other words, the cash transfer group kept money at home while the savings default group kept it at the bank. Inkind savings is somewhat lower for those who received direct deposit, though the difference is not statistically significant (column 4). Most tellingly, the effect of the savings default on total savings in column (6), is small relative to the mean in the cash transfer group and not statistically different from zero. In fact, we can rule out that savings defaults either increase total savings by more than 0.12 standard deviations or decrease them by more than 0.14 standard deviations relative to the cash treatment group.

While total savings did not change, the mix of formal and informal savings did. We examine expenditures to learn whether savings defaults affect welfare by changing consumption patterns.

We are interested in the magnitude and composition of expenditures by cash and savings default recipients. Table 6 reports spending in total and on four mutually exclusive and exhaustive categories: food, non-durables, durable goods, and transfers and fees.<sup>9</sup> We find

> 9Transfers and fees include spending on ceremonies, funerals, school fees, loans given, formal insurance, fines, and government fees.

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area among signatories covered by forest in 2000, the number of signatories that previously signed agreements with environmental provisions and an indicator for a positive numbers thereof, numbers and indicators of signatories in Africa, North America, Latin America, Europe, East or Southeast Asia, Central or South Asia, and Australasia and the Pacific, and finally, country indicators for agreement membership.<sup>7</sup> Because of the high dimensionality of this set of covariates (e.g. there are more than 100 country indicators alone), straightforward logistic estimation is not feasible. However, any _ad hoc_ variable selection performed _ex ante_ opens up our experimental design to concerns about selection bias in our matched sample arising from our specification choices.

We attempt to remove ourselves from the model selection via the use of a least absolute shrinkage and selection operator (LASSO) for our logit model selection and estimation. Logit LASSO estimation is a form of penalized maximum likelihood estimation where the penalty function is the _l_ 1-norm of **_β_** coefficients in Equation (3). This penalty functions as a model selection criterion as extraneous covariates will be dropped from the model to avoid incurring the penalty. Formally, LASSO solves the following optimization problem: where _l_ ( _·_ ) is the logit log-likelihood function, **_β_** = _{β_ 1 _, β_ 2 _, . . . , βk}_ and _∥_ **_β_** _∥_ 1 denotes the _l_ 1-norm of **_β_** (i.e.<sup>�</sup><sup>_k_</sup> _j_ =1<sup>_|βj|_).</sup><sup>_λ_istheso-calledregularizationparameterthatcontrolsthepenaltyonthe</sup><sup>_l_1-</sup> norm of **_β_** and the corresponding shrinkage. In principle, _λ_ is chosen by the researcher, however we adopt an automated approach to _λ_ selection. Our preferred _λ_ minimizes the mean cross-validation error which provides a good balance of model parsimony (from the LASSO procedure) and model

fit (necessary for subsequent propensity score matching).<sup>8</sup> We also conduct sensitivity analyses on

> 7Our biodiversity index comes from UNEP (2007). Furthermore, many countries are already members of common markets over our sample period and hence always sign the same agreements. We drop these perfectly multicollinear country indicators, only keeping one indicator per trading bloc.

> 8Table A2 presents the covariates selected (and the coefficient sign in the logit model) across a range of values for _λ_ . This table includes only covariates that are ever chosen in the Lasso procedure in any of the penalty values and does not provide an exhaustive list of all candidate covariates. Selected covariates notably include the (maximum) biodiversity index among signatories, the percent of signatory land area that is forested, whether any signatories have previously signed an RTA with environmental provisions, whether any signatory is from Latin America, the number of North American signatories, the date that the agreement is signed, and finally, a variety of country indicators. Our analysis proceeds with _λ_ = 0 _._ 26—the value that minimizes the mean cross-validation error.

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borrowers may have substantial inside information about each other’s quality.

# **5.3 Loan Repayment**

We now turn to the critical question of loan repayment. We note that the joint liability structure will in theory induce both better screening (demonstrated above), but also greater monitoring efforts. Our empirical design does not distinguish between the two potential causes of improved repayment, but rather estimates the combined causal effect.

Table 3 presents OLS estimates of Equation 2, where the outcome of interest is a dummy variable for a missed payment. This dummy variable indicates whether the client failed to make a repayment for a particular month. Saath Microfinance clients are required to make monthly repayments until the principal balance is paid in full, beginning 30 days following disbursement. Hence, the dependent variable takes on the value 1 for a particular month if the total amount repaid by the borrower for that month is nil, and 0 otherwise. We use this dummy variable as our first measure of monthly loan repayment discipline.

In our sample, almost 20% of individual liablity and only 0.1% of group-liabilty monthly loan repayments were not made. Our results in Table 3 indicate that under the group liability contract, monthly loan repayments are about 6% less likely to be missed relative to individual liability, significant at the 5% level. Controlling for other factors such as time trends and individual characteristics does not these results.

As a further robustness check, we conduct a direct “falsification” test of our analysis by using data from our clients’ previous individual-to-individual loan renewals. The sample is reduced since many clients did not have multiple individual loans in the past. Table 4 presents these results and shows no significant effect on missed payments.

Another concern over our empirical strategy is in the sample selection; since our sample consists of individual liability clients who chose to renew their borrowing under the group liability setting, these clients may be better at repayment than borrowers who did not want to enter into a group liability loan contract. However, our analysis focuses exclusively on those who renew, and includes individual fixed effects. Hence, an interpretation of our results is that even “good” clients exhibited higher repayment discipline under the group liability setting, in comparison to the individual liability setting.

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FIGURE 13

# BRAZIL SAVING RATES

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<!-- Start of picture text --> od Mahmud-E Eraqi2 P -<br>a»; a io Ghazni4ad=i M Welambar day.be<br>” :<br>oP SS ps phal<br>Mi<br>GDP per capita (US$, 2016)<br>< 100 hakhapatnam:<br>101 - 150 a<br>151 - 342<br>ia 343 - 581 \Chennai f<br>GNHO 582 814 -- 1087 813 = ;{'<br>GE 1088- 1583 ol a<br>HM 1584- 2257 a .<br>HE 2258- 3733 Colo Py 1<br>HE > 3734 A<br>Disputed<br>0 250 500 1,000 Kilometers<br>[se es os S|<br><!-- End of picture text -->
in living standards over time, even when using consumption as the welfare indicator. So the lags in implementation have bearing on the performance of PMT in reducing current poverty.

We have panel data for a subset of our study countries, namely Ethiopia, Malawi, Nigeria, Tanzania and Uganda. By exploiting the panel data, we can introduce a 1 to 2 year lag in the implementation of PMT. The precise lags are one year for Uganda, and two years for the other countries.<sup>46</sup> In other words, we develop the PMT on the Round 1 survey data and then apply it in Round 2. If anything, our lags appear to be less than found in practice.<sup>47</sup> We consider two types of lags. In the first (Method 1), we take the regression parameters from Round 1, but use the covariates from the Round 2 data. Here there is no lag in the observations of the covariates; the lag is only due to the need to estimate the PMT scores. In the second (Method 2), we simply use the PMT score from Round 1, which we then compare to the survey data on consumptions in Round 2. The lag then applies to all aspects of the PMT method (both parameter estimates and covariate values).

The targeting errors obtained using Methods 1 and 2 are found in Tables 15 and 16, respectively. Comparing the results in Table 15 (top panel) with Table 5 we see that allowing for lags increases the targeting errors on average.<sup>48</sup> For the lower line, we now find that, on average, about half of those predicted to be poor are not in fact poor based on the survey data (a mean IER of 0.553, as compared to 0.481 from Table 5). Exclusion errors are also affected, though these errors rose less markedly. Using the Extended PMT we also find a substantial increase in the targeting errors, especially for inclusion, when we allow for lags using Method 1. A similar pattern is found for Method 2.

In Table 17 we give the targeting differentials. Allowing for lags, we find mixed results. Ethiopia and Nigeria have better pro-poor targeting with lags, while Malawi, Tanzania and Uganda see increases in targeting of the non-poor. Malawi in particular has negative TD’s, indicating that the correction for lags now means that a uniform (un-targeted) policy would do better.

The post-transfer poverty rates allowing for lags are provided in Table 18. PMT still brings the poverty measures down, but by about two percentage points less when allowing for lags. For example, allowing for lags achieves an average post-transfer headcount index of 19% instead of 17%. The stylized categorical targeting schemes now attain similar or somewhat lower post-transfer poverty rates. On

> 46 <mark>The survey years are as follows: Ethiopia 2011/12 and 2013/14; Malawi 2010/11 and 2013; Nigeria 2010/11 and 2012/13; Tanzania 2010/11 and 2012/13; Uganda 2010/11 and 2011/12.</mark>

> 47 For example, recall that the mean lag between the survey year and the release date of the Progress out of Poverty Index is 3.9 years (Introduction).

> 48 Switching to the panel samples changes the targeting measures somewhat but the following observations still hold.

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