rafmacalaba/datause-encoder-data huggingface dataset:
whether the different household characteristics differ across the four assignment groups. We do this by regressing each characteristic on three indicator variables that reflect the survey assignment (the fourth group being the base category) and test for joint significance of the coefficients using an F test. For most household characteristics, the difference is insignificant, reflecting the random assignment during the field work. Only in three cases do we observe a significant difference between groups, indicating that households assigned to the detailed self-report and short proxy surveys turn out to be slightly larger and own slightly more land than the other two groups.

Turning to the 566 children, we classify them on the basis of the survey assignment they receive. This is the combination of the module assigned to the household and sub-household assignment of the child. Children were randomly selected from among all members age 10 and older to self-report or be reported on by proxy. In three cases, children selected to self-report were unavailable and their labor information was collected by proxy respondent. Omitting these children, rather than reclassifying them to their actual assignment as we have done in our analysis, has no effect on the results presented below.

To test the random nature of the assignment, we follow the same approach as for households. The results, reported in Table 2, show that we find no difference across the four assignments, except for household size, with the households assigned to the detailed self-report and short proxy surveys slightly larger. Consistent with the design of the survey experiment, there are more households with proxy reported children (Table 1 columns 2 and 4) and more individual children who are proxy reported (Table 2 columns 2 and 4). This is because proxy respondents can only be adults age 15 years and older. Thus, in households selected to the proxy assignment, children age 10-14 have a higher probability of being selected to be proxy subjects than to be selfreports, compared with children in households selected to the self-report assignment.

# **4. Results**

We present the results in three parts. In the first part, we examine differences across the children for three key statistics: their labor force participation (LFP) rate, their 12
# **The Long-run Impact of Orphanhood**<sup>**1**</sup>

Kathleen Beegle The World Bank Joachim De Weerdt E.D.I., Tanzania Stefan Dercon Oxford University Keywords: HIV-AIDS, orphans, health, education, panel data JEL-codes: O15, I10, I20, I31

> 1 This analysis was supported by the Trust Fund for Environmentally & Socially Sustainable Development at the World Bank and the Economic and Social Research Council, United Kingdom. The views expressed here do not necessarily reflect those of the World Bank or its member countries. We thank John Cockburn and seminar participants at the AAEA annual meetings 2006, Child Health in Developing Countries Workshop (Bristol, UK), IFPRI, IUSSP seminar on HIV/AIDS and Poverty, Mini-conference on Development at the University of Laval, Oxford University Development Economics Conference, PAA annual meetings 2005, Research and Analysis Working Group (Dar es Salaam), and the World Bank for very useful comments. Please address correspondence to kbeegle@worldbank.org.
OZIER - REPLICATION REDUX – p. 18 of 41 not come into existence until 2000 (ISRCTN 2018). Now, of course, many in the discipline of economics have started considering whether, when, and how it makes sense to register experiments and to specify analytical designs in advance (Olken 2015, Coffman and Niederle 2015, Anderson and Magruder 2017, Fafchamps and Labonne 2017).<sup>16</sup> Another reflection on scientific norms: unlike in an efficacy trial of a new medication, it is difficult to imagine how double‐blinding would be possible for many experiments in the social sciences. While it may be possible to obscure the treatment status of study participants so that field data collectors may be blind to it in some cases, treatment and comparison groups generally know what they are receiving. Yet a third epistemological issue: in the social sciences, studies regularly sample from a large population of interest, making CONSORT‐compliant diagrams—a standard for communicating randomized trials in medicine—more complicated to depict (Schultz, et al. 2010).

The back‐and‐forth between the replication authors and the study authors, while sometimes reading as a tense disagreement, is for the most part a polite and gracious scholarly exchange.<sup>17</sup> Aiken, Davey, and colleagues thank Miguel, Kremer, and colleagues for their openness with data and assistance with aspects of the replication; Hicks, Miguel, and Kremer, in turn, thank the replication team for identifying issues in the analysis that could be resolved in the public replication data. So why the apparent conflict of the “worm wars?” Below, I go into some detail describing the two replications, their findings, and how those findings were communicated.

# 3.1. Pure (verification) replication

The replication report’s abstract makes the pattern of results sound complicated and nuanced: _“We_ _noted various discrepancies between the published results and those from this reanalysis. These ranged_ _in importance from minor (for example, rounding errors) to moderate (for example, inaccurately labelled_

> 16 Norms are changing in economics as in other disciplines: the American Economics Association began offering trial registration in 2012, for example (American Economic Association 2018).

> 17 Much of the exchange is documented in the documents both available online at 3ie’s website and published subsequently in the International Journal of Epidemiology; these materials are cited in the bibliography at the end of this paper.
# References

- Aldrich, John H. 1993. “Rational Choice and Turnout.” American Journal of Political Science, 246–78.

- Alvarez, R. Michael, and Thad Edward Hall. 2004. Point, Click, and Vote: The Future of Internet Voting. Brookings Institution Press.

- Alvarez, R. Michael, Thad E. Hall, and Alexander H. Trechsel. 2009. “Internet Voting in Comparative Perspective: The Case of Estonia.” PS: Political Science & Politics 42 (03): 497..

- Alvarez, R. Michael, and Jonathan Nagler. 2000. “Likely Consequences of Internet Voting for Political Representation, The.” Loy. LAL Rev. 34: 1115.

- Arnstein, Sherry R. 1969. “A Ladder Of Citizen Participation.” Journal of the American Institute of Planners 35 (4): 216–24.

- Avritzer, Leonardo. 2006. “New Public Spheres in Brazil: Local Democracy and Deliberative Politics.” International Journal of Urban and Regional Research 30 (3): 623–37.

- ———. 2009. Participatory Institutions in Democratic Brazil. Johns Hopkins University Press. Bélanger, France, and Lemuria Carter. 2011. “The Impacts of the Digital Divide on Citizens’ Intentions to Use Internet Voting.” International Journal On Advances in Internet Technology 3 (3 and 4): 203–11.

- Best, Nina Juliette, Manuella Maia Ribeiro, Ricardo Matheus, and José Carlos Vaz. 2010. “Usando a Internet Para a Participação Cidadã: As Experiências de Orçamento Participativo Digital No Brasil.” Cadernos PPG-AU/UFBA, Vol. 9, Edição Especial Democracia E Interfaces Digitais Para a Participação Pública.

- Bochsler, Daniel. 2010. “Can Internet Voting Increase Political Participation.” Remote Electronic.

- Borowski, Edson Moraes. 2012. “O Desequilíbrio Fiscal Do Estado Do Rio Grande Do Sul Causas, Políticas de Ajuste E Os Efeitos Sobre a Sociedade Gaúcha.” Dissertation, Porto Alegre.

- Brandtzæg, Petter Bae, Jan Heim, and Amela Karahasanović. 2011. “Understanding the New Digital divide—A Typology of Internet Users in Europe.” International Journal of Human-Computer Studies 69 (3): 123–38.

- Breuer, Anita, and Bilal Farooq. 2012. “Online Political Participation: Slacktivism or Efficiency Increased Activism? Evidence from the Brazilian Ficha Limpa Campaign.” Evidence from the Brazilian Ficha Limpa Campaign (May 1, 2012). .

22
(t-statistic = 1.81) in Dodoma to -5.36 (t-statistic = 1.71) in Lindi. The export ban is associated with a 3.29 percent monthly price decline in Dar es Salaam, which translates into a 20 percent cumulative price decline if a ban is in effect for six months. Of the seven markets whose prices are not affected by the ban, four are in Tanzania’s Southern zone (Mbeya, Songea, Iringa, and Morogoro); Tabora is in the Central zone; and the other two are the southernmost port (Mtwara) and the northernmost port (Tanga). Markets in the Southern zone are remote maize surplus markets with prices considerably lower than elsewhere; these features are likely to attenuate the impact of an export ban. In the southern ports, as well, prices are unlikely to reflect the full impact of official trade restrictions, because market participants can circumvent formal trade channels (FEWSNET (2008),FEWSNET (2014)).

Export bans have been studied elsewhere, both in the context of domestic-world price linkages and as a cause of the 2008 and 2011 food price spikes. Ihle et al. (2009) examined the influence of export bans on Tanzanian food prices and concluded that, in contrast to our results, the influence on markets was larger in the Southern than in the Northern zone. Our results may differ from theirs because we use observed export ban dummies instead of estimating the latent influence of unobserved export bans, or alternatively, because we account for weather shocks and harvest cycles. Götz et al. (2013) examined the effects of Russia’s and Ukraine’s export grain policies during 2007/08 and 2010/11 using a Markov switching model, concluded that such policies reduced the degree of integration with world markets and also increased domestic price variability. Further, numerous authors have noted that restrictive export policies were key contributors to the price spikes of 2008 and 2011 (see, among others, Timmer (2008); Abbott (2012); and Martin and Anderson (2011)).

# **Seasonality**

We measure and control for the likely impact of harvest cycles on maize prices by employing a trigonometric specification that captures periodicity in the price time series (Shumway and Stoffer (2011)). We find that in most markets at least one of the two seasonality parameter estimates differs significantly from zero at the 5 percent level. Yet the magnitude of the seasonal changes differs across markets and zones. Even for Southern zone markets that exhibit strong seasonal patterns, the magnitude of the seasonal influence differs across markets. Prices in Songea begin increasing in September and reach their peak in February. As the harvest approaches, prices increases first moderate, and then prices fall rapidly from April through June (they decline nearly 6 percent during these months). On a cumulative basis, harvest cycles cause prices to be 20 percent lower in June than in February, and 20 percent higher in December than in August. This is consistent with a 40 percent gap between the lean season peak and the harvest season bottom.

13
distribution is usually accompanied by a low incidence of wage changes below this point, while there is little or no evidence of a similar lack of mass at small wage increases. This clearly suggests that most of the observed nominal wage freezes reflect downward rigidity. We should note that the prevalence of wage cuts in the survey that the current study is based on is also extremely rare. Only 2.3% of sampled firms cut base wages of at least some employees during the five-year period prior to the survey, while 9.6% of firms froze base wages.<sup>6</sup> In theory, wage indexation could also impose upward rigidity in addition to downward rigidity. Indeed, if firms are equally likely to be hit by positive and negative economic shocks then the rigidity imposed by wage indexation might be symmetric. However, indexation mechanisms are generally disconnected from the wage-bargaining calendar and present an asymmetric structure. As an example, in a country like Belgium, where wage indexation is most prevalent, real wage increases due to tenure or performance are negotiated and implemented. Independently from this, wages are automatically indexed either at fixed points in time or with fixed amounts of 2%.<sup>7</sup> In Spain, the common indexation clauses are independent of other wage increases and only apply upward. We conjecture from this that our indexation-based measure of real wage rigidity more probably reflects downward rather than upward rigidity.

To validate the use of the survey-based measures of downward nominal and real wage rigidity presented here, we compared our measures with the ones obtained by earlier studies in this area. It appears that the indicators defined in the current study are highly correlated with measures of downward nominal and real wage rigidity that are derived from household surveys and administrative data on individuals on the basis of the observed wage change distributions. The correlation between the country indicators in Dickens et al. (2007) and the country averages of our indicators is 0.68 for nominal and 0.61 for real wage rigidity.<sup>8</sup> Messina et al. (2009) report measures of DNWR and DRWR for 13 sectors in 3 of our countries: Belgium, Spain and Portugal. We have tabulated our measures of rigidity for those sectors and computed the correlations with the average rigidity in each sector and country during the 2000s from Messina et al. (2009). The correlation of sector averages is 0.82 for downward nominal and 0.86 for downward real wage rigidity. The high correlations in the case of downward real wage rigidity either indicate that this type of wage rigidity is to a large

> 6 The employment-weighted average share of workers who experienced wage cuts was 0.8%. 7 Recently however, all-in clauses have been included in a limited number of agreements, making real wage increases conditional on the difference between expected inflation and ex post indexation. 8 Evaluated for six countries: Austria, Belgium, France, Greece, Italy and Portugal.

9
sample, December 1975. They find that the overlap between this sample and the actual sample in the database is between 53% and 85%. Seven companies that would have been included when applying the selection criteria in 1975, were not trading on the exchanges in 1980. They argue that the survivorship bias is small in the sample. While the reported statistics about the overlap<sup>of</sup> the samples and delistings are suggestive, the extent of the survivorship bias is difficult to estimate without recreating each market's sample with a non-anticipatory inclusion rule over the 1975-1980 period. Even if this were done there is another potential survivorship bias in that the initial set of emerging markets were chosen on the basis of information available in 1980. There may have been markets that would have been included in 1975 which performed poorly between 1975 and 1980 (i.e., failed to emerge) and were thus not included in the sample.

As illustrated in Table 2, the average number of firms ranges from 11 (Zimbabwe) to 66 (Indonesia). The capitalization (as of December 1992) of the stocks included in the database ranges from $268 million (Zimbabwe) to $66 billion (Mexico). Average monthly turnover (volume for month t divided by the capitalization of the market in month t-1) for the sample period is the lowest for Nigeria at 0.05% and is the highest for Taiwan at 23.66%.

Table 3 reports some statistics for the return distributions of the IFC emerging market indices. The average monthly rate of return, in $US, (column 2) is the lowest for Indonesia (-1.02%) and the highest for Argentina (5.66%). The variability of the index returns is also quite high. Jordan has the smallest monthly standard deviation of 5.17% while Argentina has the largest monthly standard deviation of 30%. The S&P 500 portfolio, by contrast, has a monthly standard deviation (over the January 1976 - December 1992 period) of 4.46%.

11
_er.._ -

-*+ -

-

-

*

:;- .-Table

# 3.3 (ctd.) Categorical **fungibity** in India

|Co|efficient on||
|---|---|---|
|Change<br>Sector aid|Other aid<br>Total|<br>Ratio|
|in aid|(3)<br>aid|(4)1(l)|
|(1)<br>(2)|<br>(4)||
|Agriculte<br>. --<br>0.17;<br>0.07|0.10<br>0.16|<br>0.94|
|.<br>F.oodesubsidies<br>0.01<br>-0.00|0.07<br>0.07|<br>11.76|
|Ind.u-s-t-:<br>0.32<br>-0.07|0.02<br>0.10|<br>0.30|
|:<br>Energy<br>030<br>0.13|-<br>0.04<br>0|_0.55_|
|Transporzand<br>**0**<br>.<br>.10<br>0.01<br>--,communications|0.06<br>0.07|0.86|
|Other<br>010<br>_'o0.09_|0.35<br>0.44|<br>4.31|
|TottE<br>100<br>0.36|0-.64<br>'<br>1.00|<br>1.00|
|%<br>,k,e,,,<br>,6e=,<br>iD.|..-730.||
|<br> <br>__,.O_.<br>,<br>.<br> <br>|0..<br>|...<br>|
|Hiipo<br>e<br>-.<br> <br> ''|0.0|ma.|
|;~~~oe<br>.-,f**,**.<br>._<br> <br> <br>**<br> <br> <br>.-<br>Y'i<br>;!W<br>:,..-|<br> <br>0".|<br> <br>.: -;-->=|
|B<br>or ow n<br>_.::_<br>1...<br>..<br>--<br>< 7<br>-<br>::•..:<br>-<br>.<br>.<br>^=i::-<br>fi<br>.-<br>p.(1993. : '<br>.<br>-|4.4|<br>-<br>:.-L|

So far we have discussed the results of these studies as regard to aggregate fungibility. Analysis of the sectoral effects shows that sectoral expenditure increases by nearly or more than the value of aid allocated to that sector in all but one case (industry in Kenya). However, only in one case (other for Indonesia) is the increase attributable to sector-specific aid as large as the increase targeted at that sectr. ln the odier cases the remainder (which is as often as not the larger part) comes from other aid. These results are evidence of categorical fimgibility. First, because sector aid is apparently not fully used in that sector and, second, because other aid increases sectoral expenditure. But some of the increase must, at least in the Indonesian case, come from higher revenue. It is curious that a revenue term is not included in the expenditure regressions. Use of the fidl simultaneous model, incorporating the budget constraint, as suggested _58_
Cadena et al. (2013) show that remittances played an important role in reducing poverty in Central America between 2000 and 2010. However, the study shows that, in general, the overall impact has been limited for two reasons. First, remittances are more likely to be received by households in the upper part of the income distribution, which reduces the impact on poverty.<sup>26</sup> Second, remittances decreased considerably as a result of the Global Financial Crisis (Figure 13a), serving to augment the impact of this crisis on the economies of Central America.

While there is a general consensus in the literature regarding the impact of remittances on poverty, less consensus exists with respect to their impact on inequality. For instance, McKenzie (2004) shows that remittances decreased inequality in Mexico, while Adams (2005) and Barham and Boucher (1998) show that remittances increased inequality in Ghana and Nicaragua, respectively. Acosta et al. (2008) show that remittances had an equalizing impact in nine out of 11 countries in Latin America, with Nicaragua and Peru being the exceptions. However, the authors find that changes in the Gini coefficient attributable to remittances are relatively small since remittances are largely directed to relatively better-off households.

In order to analyze the impact of remittances on per capita income inequality, we study the cases of Mexico, Honduras, El Salvador, and the Dominican Republic - countries for which remittances are well captured in household surveys. These countries represent good case studies since remittances represent a relatively large shared of GDP and per capita household income (Cadena et al. 2013). These countries also represent different evolutions of per capita income inequality in the region - the Gini coefficient decreased in El Salvador and the Dominican Republic over the entire period under analysis, while in Mexico and Honduras decreased between 2003 and 2010 and increased after 2010.

Consistent with the fact that remittances are received by households in higher income quintiles, a decomposition of changes in income inequality shows that changes in remittances increased inequality in three out of the four countries under analysis between 2003 and 2010 (Figure 14). Similarly, inequality has also increased due to changes in remittances in three out of the four countries analyzed as the flow of remittances recovered in the post-crisis era – the exception is the Dominican Republic. Interestingly, this is the only country of the four analyzed in which remittances have fully recovered from the crisis. It is important to note that the impact of remittances on income inequality is relatively low if compared to the impact of other sources of income. For instance, remittances contributed only 15 and 10 percent of the growth in the Gini coefficient in Mexico and Honduras in 2010-2012, respectively.

> 26 This is partially due to biased self-selection into migration. For example, Chiquiar and Hanson (2005) find that Mexican immigrants are on average higher-skilled than non-immigrants.

21
this exercise is to measure the effect of size-dependent distortions in the presence of bribery and to compare it with the previous literature. In the second quantitative exercise, I calibrate model parameters including distortion rates and the fix cost of bribery by taking advantage of the bribery payment data for Türkiye from the WBES. The goal of this exercise is to measure the level of distortions as well as the role of bribery in an economy with distortions.

The U.S. exercise shows that bribery opportunities decrease the negative effects of sizedependent distortions on the mean plant size and on the output. Since bigger plants have more resources to spend on bribery, they are able to circumvent the size dependency of distortions. Hence both small and big plants are subject to similar distortion levels after bribes.

For the second quantitative exercise, I use the data on bribery payments of big and small plants, as well as the plant size distribution of Türkiye, in order to calibrate key parameters of the model including the size-dependent distortion rate and the return on the bribe parameter.

My results indicate that the inferred distortion levels are sizable: plants are subject to a distortion rate of 28.3% after the inclusion of bribery payments. Small plants pay almost all of their bribe for the associated fix costs since their estimated return on bribe is low. On the other hand, the return on bribes is high enough for big plants since they are subject to higher distortion rates.

Finally, removing size-dependent distortions, and so the incentives for bribing, results in substantial increases in output and mean plant size. Since the size-dependent distortions affect bigger plants more than small plants, bigger plants increase their input demand more than small plants by the removal of distortions. As a result, if distortions associated with being assigned to a corrupt official were removed, aggregate output and mean plant size would grow by 63.6% and 82.5% respectively.

The rest of the paper is organized as follows. The next section provides a concise literature review. Section 3 describes the data sets used and summarizes descriptive facts related to bribery and plant size in the US and Türkiye. Section 4 presents the model and derives key equations to compare the different steady-state equilibria. Section 5 describes the calibration of the parameters and discusses the model’s behavior with the calibrated values. Section 6 presents counterfactual experiment results, and Section 7 concludes.

3