rafmacalaba/datause-encoder-data huggingface dataset:
and employment, as well as on defect rates, inventory levels, and energy usage. The final source of data comes from linking firms to administrative data sources on employment and exports.

Obtaining data from the firms was difficult and complicated by several factors. First, a consequence of poor management is that firms did not routinely and consistently keep records of some KPIs. Firms would change the units of measurement at times from pesos to physical units, and the type of physical unit they used (e.g. from number of items to kilograms).<sup>11</sup> Second, data collection in the firms was conducted during on-site visits by CNP. We hired Innovations for Poverty Action to provide an independent check on this data, and to help in extracting data from the firms – this included oversight of both the management practice data and the KPI data. But CNP had breaks in its contracts, which meant data collection halted for months at a time, and they had a long list of KPIs they wanted from firms, which increased the burden on firms of reporting. The result was that some firms dropped out of providing follow-up information, even after repeated follow-up visits seeking just a few key variables. Third, ten of the firms closed during the course of the study (4 control, 3 individual treatment, and 3 group treatment, p-value of equality of death rates 0.911).

These three factors mean that we only have both employment and sales data through to December 2017 for 105 firms (69% of the sample), comprising 33 control firms, 37 individual treatment firms, and 35 group treatment firms (p-value of equality of attrition rates is 0.744). Table A4.2 compares the baseline characteristics of these firms to those that attrit, and shows that we cannot reject equality of means. Moreover, balance on baseline observables for those firms which do report is similar to our balance on the overall sample. Nevertheless, we use firm fixed effects in our estimation of impacts on firm outcomes to control further for any time-invariant differences among firms.

For employment outcomes, we can also use the PILA (Unified Register of Contributions), which is the national information system used by firms to file the mandatory contributions to health, pensions, and disability insurance paid for workers. This data has the advantage of covering more of the firms, since we could match 156 of the 159 firms to these records. Moreover, it is more comprehensive in length, enabling us to track firms from pre-intervention (January 2013), right

> 11 These changes in units also occurred because firms would produce different products at different times, depending on what orders they received.

13
**Table 1: Estimates of the impact of market access on cropland**

||(1)<br>OLS|(2)<br>OLS|(3)<br>FE|(4)<br>FE|
|---|---|---|---|---|
|_Ln MAt-_1|0.185***|0.035***|-0.025***|0.018***|
||(0.00)|(0.00)|(0.00)|(0.00)|
|_Avg. rainfall t_||0.644***||-0.071***|
|||(0.00)||(0.01)|
|(_Avg. rainfallt_)<sup>2</sup>||-0.063***||0.002***|
|||(0.00)||(0.00)|
|_Ln pop. densityt-1_||1.241***||-0.708***|
|||(0.01)||(0.02)|
|_Ln dist. to major port_||-0.088***<br>(0.00)|||
|Constant|0.983***|0.497***|1.120***|1.351***|
||(0.00)|(0.04)|(0.00)|(0.01)|
|Country×year dummies|No|Yes|||
|Observations|1,161,664|1,160,235|1,161,664|1,160,235|
|Number of groups|||290,416|290,130|
|R-squared|0.073|0.482|0.000|0.010|

Notes: This table presents estimates from OLS (columns 1 and 2) and fixed effect (columns 3 and 4) regressions of the natural logarithm of cropland area at time _t_ on the natural logarithm of the lagged market access index ( _Ln MA t-_ 1). Controls included in the OLS regression (column 2): average rainfall over the period ( _Avg. rainfall t_ ) and its square, natural logarithm of lagged population density ( _Ln pop. density t-1_ ), natural logarithm of distance to nearest major port ( _Ln dist. to major port_ ), country dummies, year dummies, and country × year dummies. Controls included in the FE regressions (column 4): period average rainfall and its square, and natural logarithm of lagged population density. Robust standard errors are in parenthesis, where *** is significance at the 1% level, ** significance at the 5% level, and * significance at the 10% level.

We now turn to the estimation of the impact of the change in the market access on the change in cropland area (Regression 5). Under this specification, doubling of the market access index is associated with an increase in cropland area by 6.3 percent.<sup>9</sup> This is more than 3 times the impact estimated in levels under Regression (4). Note that in Regression (5), we have introduced a dummy variable for cells where cropland had been decreasing in the previous period. We find that for these cells the improved market access actually accelerates the reduction in cropland area.

12
|**Country**|**Survey(s)**|**Year(s)**|
|---|---|---|
||Integrated Household Survey|2000-06|
|Mexico|Encuesta de Gastos de Hogares|2000, 02, 04-<br>06|
|Micronesia|Income and Expenditure Survey|2005|
|Moldova|Household Budget Survey|2001-08|
|Mongolia|Income and Expenditure Survey|2005|
||LivingStandard Survey|2000,05|
|Montenegro|Integrated Household Survey|2001-03|
|Morocco|Enquête de vie des ménages|2006|
|Mozambique|Inquérito aos Agregados Familiares|2002|
|Myanmar|Income and Expenditure Survey|2002,06|
|Namibia|Income and Expenditure Survey|2003|
|Nepal|LivingStandard Survey|2003|
|Nicaragua|Encuesta de Hogares|2001,05|
|Niger|Enquête Budget-Consommation|2007|
||Enquête sur le conditions de vie|2005|
|Nigeria|LivingStandard Survey|2003|
|Pakistan|Integrated Household Survey|2001|
|Panama|LivingStandard Measurement Survey|2003|
||Encuesta de Hogares|2000-06|
|Papua New Guinea|Income and Expenditure Survey|2005|
|Paraguay|Encuesta de Hogares|2000-07|
|Peru|Encuesta de Hogares|2000-07|
|Philippines|FamilyIncome and Expenditure Survey|2000,03,06|
|Poland|Household Budget Survey|2000-02, 04-<br>06|
|Romania|Household Budget Survey|2003,06-07|
||FamilyBudget Survey|2001-03|
|Russia|Household Budget Survey|2000-04, 06-<br>07|
|Samoa|Income and Expenditure Survey|2002|
|São Tomé and<br>Principe|Enquête sur le conditions de vie|2000|
|Senegal|Enquête auprès des ménages|2001|
|Serbia|Household Budget Survey|2003-04, 06-<br>08|
||LivingStandard Survey|2003|
|Seychelles|Household Budget Survey|2006|
|Sierra Leone|Integrated Household Survey|2003|
|Slovenia|Household Budget Survey|2000,04-05|
|Solomon Islands|Income and Expenditure Survey|2005|

19
welfare losses as of early June, for any plausible _α_ .<sup>24</sup> This implies that doing nothing was a dominated policy response in many countries, at least if the epidemic progressively disappears after early June and if Covid-induced poverty lasts for one year only.

This nding ensues from Figure 5, which shows break-even _α_ ̃ under saturation mortality and with poverty computed for income class-specic poverty thresholds, as before. The gure uses the baseline growth estimates and the distribution-neutral growth assumption. The graph shows that break-even _α_ ̃ are less than one in almost all developed and in most developing countries. But, as we saw in Section 2, _α_ is theoretically bounded below at 1 , so the estimated welfare outcomes are worse under no-intervention for all admissible normative criteria.

<!-- Start of picture text --> 500 1000 2000 5000 10,000 20,000 50,000 100,000<br>GDP per capita (PPP, constant 2011)<br>1.9$ poverty line<br>3.2$ poverty line<br>5.5$ poverty line<br>21.7$ poverty line<br>10<br>1<br>0.1<br><!-- End of picture text --> Figure 5: Break-even _α_ ̃ in all countries as of early June 2020 (baseline, distributionneutral contraction, no-intervention scenario with saturation, group-specic poverty thresholds) We argue that the sub-optimality of no-intervention in developed countries is robust to taking less conservative poverty estimates. First and foremost, we assume conservatively that the no-intervention scenario has zero poverty costs, which is implausible. Second, if we relax our assumption that additional poverty only lasts for one year, and assume that the current poverty costs are in fact two or three times larger than our estimates, the result still holds for developed countries. Indeed, as shown in Table 3, the median break-even _α_ ̃ for this group of countries is never larger than one-third under the various scenarios considered. In the case of upper-middle income countries, the median breakeven _α_ ̃ is never greater than one under the various scenarios considered, which also

> 24Recall that _α >_ 1 _._

19
where _npb_ indicates Non-Bank Private, _nb_ indicates Non-Bank, _pub_ indicates Public, _j_ denotes the borrowing country, and _t_ denotes the time period.<sup>�</sup> _XBS_ is our estimated cross border bank debt, _XBC_ denotes the cross border claims (from the LBS) of BIS reporting banks, and _INTC_ is international claims (from the CBS on immediate counterparty basis). The CBS international claims are defined as the sum of XBC and the local claims by foreign affiliates that are denominated in foreign currencies (LCFC).

This construction of the split of bank debt makes the following assumptions: First, the sectoral shares for _INTC_ are the same as the sectoral shares for _XBC_ . This is reasonable since for most countries, LCFC tends to be small relative to XBC.<sup>80</sup> Second, the sectoral shares for the set of banks that report LBS data (44 countries) are the same as the sectoral shares for the set of banks that report CBS data (31 countries). The 31 CBS reporting countries account for about 90% of the XBC in the LBS, and the CBS captures the activities of the subsidiaries of banks from these 31 countries worldwide. As a result, the CBS data are sufficiently representative to make the above assumption a reasonable one. Third, data for the CBS that allows us to estimate the split of Non-Bank into Public and Private is not available for advanced economies before 2000, and is only available on a semiannual basis for EM for the period before 2000. We linearly extrapolate the semiannual shares to Public and Private into a quarterly series for EM. For advanced economies, we assume constant shares from 2000 backwards.<sup>81</sup> Having made these assumptions and constructed the external debt to bank creditors, we

> 80 While for most countries, LCFC tends to be small relative to XBC, there are a small number of exceptions. For example, this is not the case in dollarized economies (e.g. Ecuador) and some emerging European economies (e.g. Hungary and Poland), where lending denominated in euro and in Swiss francs has been non-negligible.

> 81The assumption of constant shares for advanced economies before 2000 is not too concerning when we are only extending back 4 years.

88
_t_ { − _x_ ψ′ ( _x_ | _z_ )}[ _q_ ( _x_ ) − ]1 _f_ ( _x_ ) _dx_ is initially upward-sloping. Taking the ∫ 0 derivative, ∃ _v_ < _z_ : _q_ ( _x_ ) > 1 ∀ _x_ ∈ [,0 _v_ ] . Conversely, if ∃ _v_ < _z_ : _q_ ( _x_ ) > 1 ∀ _x_ ∈ [,0 _v_ ] , _t_ then { − _x_ ψ′ ( _x_ | _z_ )}[ _q_ ( _x_ ) − ]1 _f_ ( _x_ ) _dx_ is initially upward-sloping, whence ∃ _p_ 0<sup><</sup> 1 : πJ<sup>(q│p)</sup> ∫ 0 > 0 ∀ _p_ ≤ _p_ 0 . Theorem 5 follows. From (3.12) and (2.3), − 1 _mx_ π _D_ ( _q_ ) = _x_ [ _q_ ( _x_ ) − ]1 _f_ ( _x_ ) _dx_ . Setting _q(x) = q*_ � _x > z_ in this, and using _z_ ∫ _z mx_ 1 − _<u>q</u>_ * _xf_ ( _x_ ) _dx_ = μθ , we have . μθ = π _D_ ( _q_ ) , from which Theorem 6 follows. ∫ _z z_

# **_References_**

Atkinson, A.B. (1987). On the measurement of poverty. _Econometrica_ , vol. 55, pp. 749-764. Chenery, H., M. S. Ahluwalia, C. L. G. Bell, J. H. Duloy and R. Jolly (1974). _Redistribution_ _with Growth: Policies to Improve Income Distribution in Developing Countries in_ _the Context of Economic Growth._ New York & Oxford: Oxford University Press.

Datt, Gaurav (1998). Computational tools for poverty measurement and analysis. Washington D.C.: _International Food Policy Research Institute (IFPRI) Discussion Paper No. 50_ (Food Consumption and Nutrition Division).

Essama-Nssah, B. (2005). A unified framework for pro-poor growth analysis. _Economics Letters_ , vol. 89, pp. 216-221.

Foster, J.E. and A.F. Shorrocks (1991). Subgroup consistent poverty indices. _Econometrica_ , vol. 59, pp. 687-709.

- Foster J., J. Greer and E. Thorbecke (1984).  A class of decomposable poverty measures. _Econometrica_ , vol. 52, pp. 761-766.

- Holland, Paul W. (1986). Statistics and causal inference. _Journal of the American Statistical Association_ , Vol. 81, No. 396: 945-960.

Jenkins, S.P. and P.J. Lambert (1997). "Three 'I's of poverty" curves, with an analysis of

- U.K. poverty trends. _Oxford Economic Papers_ , vol. 49, pp. 317-327.

Kakwani N. C. (1999). Inequality, welfare and poverty: three interrelated phenomena.

In Silber, J. (ed.) “ _Handbook of Income Inequality Measurement_ ”. Boston: Kluwer Academic Publishers.

29
places, the identification strategy as explained so far is expected to be weaker as we evaluate communities incorporated later in time. This effect is reinforced by the lower take-up rates among eligible households after 2001. To address this concern, we add to the baseline specification additional analyses that follow the same identification strategy, but restrict the sample in different ways. We continue to use variation in exposure between older and younger children, but only use the sample of children that live in households that, according to different criteria, are more likely to participate in the program.

# **_Time trends and community shocks_**

Also important to the identification of treatment effects are the assumptions regarding time trends and shocks. The underlying assumption regarding time effects comprises two components: how time trends change across cohort groups, and how time trends differ across locality groups.

Regarding the first component, if different cohorts were exposed to different events or shocks, the estimated impact will not be able to disentangle the effect of the program from the effect of these events. This source of bias is partially controlled for by estimating differences across cohorts in treatment communities relative to control communities. However, if there are location-specific shocks that affect differently our exposed and non-exposed cohorts of children, these effects are not accounted for.

One concern is the fact that some localities (or households) were incorporated into Oportunidades responding to specific negative shocks, in most cases hurricanes. We use administrative information about those localities, and excluded them from the analysis as a robustness check.<sup>21</sup>

> 21 Only 3 MxFLS localities were in this list, and all results are robust to the exclusion of these localities.

21
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PoLjy REsEARC\IXWORKIN4.; _PAI'FR_ 1548

# Summary findings

Drawing on interinational evidence, van Zyl, Binswanger, and Thirtle discuss the son rces of economies of scale. Ulsing representative farm-level survev data for South Africa's six mnajor grain-producing areas and one irrigation area for rhc period 1975-90, they:

* Describe the structure of South African agriculture, detailing the distributioll of larin sizes and results from previous studies of farmi-sizu e fficiency.

* Analvze the evidence on scale efficiency in the former homelands.

* Analyze the relationishiip between farm size and efficienicy in commieitrcial farminig and discuss how policy affects that relationsliijp.

Clearly policy hals a crucial impact on the relationship between farm size and efficienicy. lhey find that:

* Farms in tht iformiter homelanids seem to be scaleinefficient, which is unsurprising, givenl the historical lack of access to support services and infrastructure, policies that discriminate against farmers in the homelands, and tht extremeitlc fragimierited and limited lanid-use rights of farmerzs the _re._

There is an inverse relationship between farm size and efficiency in the commercial farming areas for the range of farms analyzed, regardless what method is used. This inverse relationship seems to become stronger and more accentuated as policy distortions - whichi tend to favor large farms over small ones - are removed.

* Large farms tend to use more capital-intensive methods of production, while smaller farms are morte labor-intensive. And managerial ability seems to be better on larger farms.

There is an inverse relationship between farm size and efficiency in South African agriculture despite South Africa's history of policies favoring relatively large mechanized farms. Clearly, efficiency gains could be significant if commercial farms became smaller. To encourage that trend, policies and distortions that favor large farms over small should be removed.

'[his papera product of the Office of the Director, Agriculture and Natural Resources Departmentis part of a large! effort in the department to design appropriate strategies for land reform. Copies of the paper are available free from tilt World Bank, 1818 H Street NW, Washlinigton, DC 20433. Please contact Melissa Williams, roonm S8-222, telephone 202458-7297, fax 202-522- 1 142, Internet address mwilliams(i)xworldbank.org. November 1995. (45 pages)

> _Thc Policv Rese.ar,_ I **_\WYorking_** _Paper Series dissemniniates the findings of work in progress to encourage the exchange of ideas about deielopment_ **_Av'_** _Anz_ **_ob,'Ltiic Is._** _of the series is toget the findings out quickly, even if the presentationsare less than fully polished. The papers c-arry tbe_ **_names_** _If tie authors_ **_atid_** _should be used and cited accordingly. The findings. interpretations, and conclusions are the_

> _authors'_ **_owU_** _'1d_ **_sb1_** _huld_ **_otl_** _be attributed to the World Bank, its Executive Board of Directors, or any of its memiber countries._

Produced by the Policy Research Dissemination Center
I

# I. Introduction

The recent boom in theoretical analyses of long run growth has sparked research and interest in cross-country empirical studies of growth. These studies typically regress the average rate of growth for a sample **of countries** on a group of explanatory variables. The variety of cross-country growth regressions is enormous. A quick glance at Table 1 indicates that authors study different sets of countries, over different years, and use different explanatory variables. The great diversity of studies makes it difficult both to discern consistent relationships and to compare the results of studies. Furthermore, the analytical problems that plague cross-country regressions make it difficult to consider any set of findings reliable.

This paper has two purposes. First, by discussing the methodological, conceptual, and statistical problems associated with large cross-country studies of growth, we hope to stimulate improvements in the design, implementation, and therefore, the interpretability of cross-country investigations. Although we do not make specific recommendations, we outline general ways to (a) enhance the econometric design of large cross-country regression analyses, (b) improve the data construction and the sample selection processes, and (c) enhance the presentation and interpretation of - cross-country studies. Also, this paper may serve as a useful though - perhaps overly detailed warning to readers of the growth literature about the confidence they should place in cross-country findings.

This paper's second purpose is to examine the particular problems associated with cross-section attempts to link macroeconomic policies with growth. Although we would like to construct objective, internationally
We provide strong evidence against the validity of the proportional hazards assumption in the Cox model. A possible explanation can be the presence of unobserved individual heterogeneity that is not accounted for. Given the nature of the trade flow data where survival rates are grouped into annual observations and there are many tied failure rates, we estimate the Prentice-Gloeckler (1978) model which provides a discrete time equivalent of the Cox proportional hazards model. We augment this with a gamma mixture distribution to address unobserved individual heterogeneity (Meyer, 1990). Our analysis reveals that accounting for unobserved heterogeneity is indeed important as both coefficients and significance levels change dramatically. In general, failure to account for unobserved heterogeneity will, if it is indeed important, over-estimate the degree of negative duration dependence in the (true) baseline hazard, and under-estimate the degree of positive duration dependence. Moreover, the proportionate effect of a given regressor on the hazard rate is no longer constant and independent of survival time and the proportionate response of the hazard to variation in each regressor at any survival time is attenuated. All of this is precisely what we observe.

Our empirical results confirm that cultural and geographic ties between trading partners as well market size and exporting experience play an important role in export survival. The results moreover suggest that exporting experience is product and region specific, particularly for developing country exporters. Using the classification proposed in Rauch (1999), we also show that, in line with standard findings in the literature, factors determining search costs as well as cultural and geographic ties between trading partners matter more for differentiated than for homogeneous products. We check for the robustness of all of these results using a range of alternative models and specifications. Finally, the importance of unobserved heterogeneity in product level export flows points to the importance of using firm- as well as product level data in understanding export survival.

The paper is organized as follows. Section 2 presents the data set and provides descriptive statistics on the global pattern of duration dependence in the data as well as differences in the determinants across product groups. Section 3 provides a brief review 3