rafmacalaba/datause-encoder-data huggingface dataset:
<!-- Start of picture text --> Election turnout Share of votes for left<br>Year Year<br>Share of votes for center Share of votes for right<br>Year Year<br>Electoral competition<br>Year<br>Figure 5. Parallel Trend Assumption – Presidential Elections<br>Discrete Treatment Variable<br>2002 2006 2010 2014 2018 2022 2002 2006 2010 2014 2018 2022<br>2002 2006 2010 2014 2018 2022 2002 2006 2010 2014 2018 2022<br>2002 2006 2010 2014 2018 2022<br>.04 .04<br>.02 .02<br>0 0<br> (95% CI) (95% CI)<br>β β<br>-.02 -.02<br>-.04 -.04<br>.04<br>.04<br>.02<br>.02<br>0<br> (95% CI) (95% CI) 0<br>β β<br>-.02<br>-.02<br>-.04 -.04<br>.04<br>.02<br>0<br> (95% CI)<br>β<br>-.02<br>-.04<br><!-- End of picture text --> _Notes:_ The figure illustrates the results of an event study estimation. We interacted the discrete variable PEP, which takes the value of one in municipalities where there are PEP holders, with presidential electoral years excluding the election of 2018, the year the PEP program was implemented. The estimates include municipality, electoral year, and department electoral-year fixed effects, and they control for the interaction between electoral year dummies and a set of predetermined municipal characteristics, measured before the beginning of our period and listed in Table C.2. Standard errors were clustered at the municipality level and bars represent a 95% confidence interval.

24
# **3. Are impact evaluations of interventions in conflict prevention and peacebuilding feasible?**

Conflict-affected settings make conducting impact evaluations challenging. To address the objections that impact evaluation of peacebuilding interventions cannot be done, and to document the type of methodologies that have been more prominently used, Samii, Brown, and Kulma (2012) conducted a thorough literature search to identify all the impact evaluations that have been conducted (and including some ongoing studies) of what they call stabilization interventions. Their search and review covers impact evaluations of peacebuilding/stabilization interventions by any donor or government. They found that there are roughly two dozen impact evaluations, some ongoing, across seven categories of stabilization interventions. While the search did not fulfill all the criteria to qualify as a systematic review according to the Campbell Collaboration guidelines<sup>2</sup> , it was extensive, covering multiple databases as well as direct contact with the researchers to identify ongoing studies. The largest number of impact evaluations has been of ex-combatant reintegration programs and of peace dividends (community-driven reconstruction) programs. The impact evaluations they found were conducted in Afghanistan, Burundi, Democratic Republic of Congo, the Aceh region of Indonesia, Israel and Palestine, Liberia, Rwanda, Sierra Leone, Sri Lanka, and Northern Uganda.<sup>3</sup> The Samii et al. search results demonstrate that impact evaluation is indeed possible of peacebuilding interventions in conflict-affected settings in a number of circumstances. This insight then brings us to a second type of concerns relating to the worth of impact evaluations. What sort of insights can these types of evaluations bring that other types cannot?

This paper addresses major concerns and questions about the feasibility, value added and ethics of impact evaluations in conflict-affected settings. It builds among others on the review of the two dozen screened studies from the Samii et al. paper, as well as insights from a survey we administered to the authors of the included studies. The paper explores (i) evaluation design issues in conflict-affected situations; (ii) evaluations as interventions, and the implications for the risks and reliability of results; (iii) the importance and value-added of impact evaluations; and (iv) ethical concerns about impact evaluations in conflict prevention and peacebuilding.

> 2 http://www.campbellcollaboration.org/systematic_reviews/index.php

> 3 Annex A lists the included studies.

4
earnings. Note that this data does not include information on worker hours; however, given the low flexibility of work hours (see Section 5.1), it is reasonable to use attendance as a meaningful measure of the extensive margin of labor supply. These administrative data are used by Olam to compute earnings, and the amount to be deposited into workers’ accounts in each paycycle.

We supplement this with data collected through two sets of phone surveys, which form the basis for our baseline data for Phases 1 and 2. These include information on perceptions about redistributive pressure. In addition, we use a more detailed in-person endline survey, which includes details about financial transfers with network members.

Table 2 provides descriptive statistics for our study sample, and checks for balance in baseline covariates across treatment arms separately for each Phase. Across treatments, the average worker in our sample has worked at the factory for 620 days, and has a baseline attendance rate of 68%. Almost all workers (98%) are women.

Our primary outcome measure, earnings, is balanced at baseline. Of the 25 comparisons presented, only the comparisons on attendance are statistically distinguishable across treatment arms at the 5% level. Note that our primary empirical specification controls for any baseline differences in levels using a differences-in-differences approach that includes individual fixed effects. In addition, as we show below, we find similar treatment effects using only endline data controlling for baseline covariates.

# **6.2 Estimation**

Our primary outcome is workers’ daily earnings (in FCFA). Given the linear piece rate incentive scheme, this is equivalent to examining effects on output, and serves as our measure of workers’ total labor supply. We also study effects on attendance to specifically examine the extensive margin decision of deciding to come to work.

We estimate effects for Phase 1 (comparing the Private treatment with Control) and for Phase 2 (comparing the Private treatment with the Non-Private treatment). To measure treatment effects, we use the administrative panel data from the factories to estimate difference-in-differences regressions at the worker-day level: where _yit_ is the outcome of interest for worker _i_ on date _t_ . The _PrivateAccti_ indicator equals one if worker _i_ was assigned to receive the Private account treatment. _Postt_ is an indicator that equals one on dates when the blocked savings account is active, and _Announcementt_ is an indicator that equals one during the announcement period (after workers are told their 22
# **Abbreviations and Acronyms**

|AERs|Annual Environmental Reports|
|---|---|
|ASRF|Ahafo Social Responsibility Forum|
|CDD|Centre for Democratic Development|
|CELD|Centre for Environmental Law and Development|
|CEPIL|Centre for Public Interest Law|
|CEPS|Customs, Excise and Preventive Service|
|CHRAJ|Commission on Human Rights and Administrative Justice|
|CSOs|Civil Society Organizations|
|DAs|District Assemblies|
|DACF|District Assemblies Common Fund|
|DCE|District Chief Executive|
|EARs|Environmental Audit Reports|
|EIAs|Environmental Impact Assessments|
|EITI|Extractive Industries Transparency Initiative|
|EPA|Environmental Protection Agency|
|ERP|Economic Recovery Programme|
|FoE-Ghana|Friends of the Earth-Ghana|
|GACC|Ghana Anti-Corruption Coalition|
|GDP|Gross Domestic Product|
|GEITI|Ghana Extractive Industries Transparency Initiative|
|GEO|Green Earth Organization|
|GNPC|Ghana National Petroleum Corporation|
|GPRS|Ghana Poverty Reduction Strategy|
|GSD|Geological Survey Department|
|IDEG|Institute for Democratic Governance|
|IDMC|Inspectorate Division of Minerals Commission|
|IEA|Institute of Economic Affairs|
|IRS|Internal Revenue Service|
|ISODEC|Integrated Social Development Centre|
|ISSER|Institute of Statistical, Social and Economic Research|
|LTU|Large Taxpayer Unit|
|MC|Minerals Commission|
|MDAs|Ministries, Departments and Agencies|
|MMDAs|Metropolitan, Municipal and District Assemblies|
|MTEF|Medium Term Expenditure Framework|
|MPs|Members of Parliament|

4
where data is available, the law does not include preferential treatment clauses against foreign bidders. A domestic sourcing provision is present in 58 percent of the sample. We find that the share of countries with protectionist laws in government procurement is lower among countries that participate in major international agreements that liberalize procurement markets, the WTO GPA and the EU, and in high-income countries. We also find that this share tends to be lower in countries with institutions of better quality, as measured by the World Governance Indicators.

To further validate the national law data and investigate the variation in trade openness across countries, we estimate the relationship between import share in total spending and the protectionism index. Because the national law data were collected during 2021-22 while the trade data cover the 2000-2018 period, and in absence of an exogenous shifter for the protectionism variables, we interpret the empirical estimates as suggestive of the correlation between trade and the protectionist character of national laws. The results indicate a systematically negative correlation between import shares and the protectionism in government procurement, which is robust to controlling for the influence of other country characteristics and different definition of government procurement in the trade data. Lower import shares in government procurement are especially observed in countries where the law provides for preferential treatment of domestic bidders. These results from cross-country regressions are confirmed in estimations of gravity models for bilateral imports. In particular, we find that the “border effect” (how much the country’s spending market is local relative to international, after controlling for standard determinants of bilateral trade) increases with protectionism in government procurement, with the effect being again stronger for preferential treatment provisions.

The empirical exercise that we propose in this paper is subject to a number of limitations. In addition to the lack of a credible identification strategy that could support a causal interpretation of the estimates, there are measurement issues in protectionism in government procurement. These can explain why our estimates reveal correlations between trade openness and protectionism as observed in the law that are imprecisely estimated, especially for some components of the law.

With these caveats in mind, our findings have important implications for government procurement policies. The relationship between protectionism in government procurement and overall trade underscores the significance of procurement laws for the sourcing decisions of domestic firms, namely those who win procurement contracts. It also highlights the possibility that the presence of this type of protectionism can well mask the presence of protectionism in other policy areas, unobserved to us, that matter for overall trade.

20
and Development (OECD) in 1989–98. They show that the main drivers of political budget cycles were the levels of government transparency and political polarization. Using data from 32 European countries in 1990–2010, <u>Enkelmann and Leibrecht (2013) find that political budget</u> cycles are typical in newly democratized countries. In contrast, voters in mature democracies penalize politicians for increasing public expenditure to enhance their chances of re-election. Using a panel of 71 countries over 1972–2009, Brender and Drazen (2013) show that politicians’ tenure may be another driver of political budget cycles and argue that to win votes, experienced politicians are more likely to change the composition of government expenditures than newcomers. A new leader might need several years to make changes in the budget composition, probably because it takes time to understand legislative procedures and bureaucratic rigidities after taking office.

<u>Castro and Martins (2018)</u> analyze government expenditures in 18 European countries in 1990– 2012. They show that governments increase public spending during election years regardless of ‐ the political party they belong to. Kyriacou, Okabe, and Roca <u>Sagalés (2022) analyze electorate</u> myopia and show that voters in a diverse sample of 67 countries prefer the immediate benefits to their consumption rather than longer-term fiscal sustainability, incentivizing politicians to implement opportunistic policies to meet voters’ demands.

The literature on the political business cycles, discussed above, does not address, however, whether political budget cycles persist in the presence of systemic shocks like a pandemic, war, or natural disaster. To our knowledge, no prior studies have analyzed whether the maturity of democracy, political competition, and the rule of law in a country remain driving factors of political budget cycles in such contexts. Also, much of the cross-country literature has not exploited an exogenous variation in the national electoral cycle across countries, which would allow for clearer identification of the effects of the political budget cycle. The shock of the pandemic, which occurred almost simultaneously across the world and was exogenous to the electoral cycle of each country, provides such variation. Our data and analysis aim to fill this gap in the literature by providing cross-country evidence on the presence, or not, of a political budget cycle in the governments’ social protection response to the pandemic.

6
- 38 -

Table 6.2 Dependent Variable is DLWAGE - Sample range: 1983(1) 1989(2); number of observatiorns: 26

|VARIABLE|COEFFICIE|NT STD.|ERROP<br>T°STAT.|2-TAIL|SIG.|
|---|---|---|---|---|---|
|DLCPI<br>|0.7908919<br>|<br>0.167<br> <br>|3248<br>4.7266867<br>|<br>0.00|0|
|DLPRO<br>|0.3075491<br>|<br>0.123<br> <br>|7486<br>2.4852732<br>|<br>0.02|1|
|ECMH(-l)<br>|-0.6369975<br>|<br>0.141<br> <br>|0623<br>-4.515717<br>|0<br>0.00|0|
|DUM844<br>|-0.0635518<br>|<br>0.025<br>|2779<br>-2.514127|9<br>0.02|0|
|DUM881|-0.0733555|<br>0.029|5827<br>-2.479670|3<br>0.02|2|
|R-squared<br>|<br>|0.603610<br>|<br>Mean of depend<br>|ent var|0.024574|
|Adjusted<br>|R-squared<br>|0.528107<br>|<br>S.D. of depend<br> <br>|ent var<br>|0.035165|
|S.E. of r<br>|egression<br>|0.024157<br>|<br>Sum of squared<br> <br>|resid|0.012254|
|Durbin-Wa<br>|tson stat<br>|1.811326<br>|<br>F-statistic<br>||7.994525|
|Log likel|ihood|62.68714||||

# 6.3 Poland

First difference changes for wage, prices and productivity are reported in Figure 6.2. The pattern of wage change is clear; adjustment is in the first quarter with the exception of 1987(1) 5'. Producer price changes exhibit a similar first quarter pattern with consumer price changes clustered generally in the second quarter. Productivity also exhibits first quarter spikes with a deceleratiou over the last eight quarters of the sample. For both wages and prices, there are sharp accelerations toward the end of the period, particularly from 1989(2) onward as a set of upward adjustments to administered prices occurs and the economy enters into a short high inflation period.

Tne descriptive statistics presented in Table 6.3 indicate a high and predictable correlation between wage and price changes, particularly for producer prices. The mean of wages is somewhat lower than of the cons'tmer prices while the sum of the producer price and productivity variable almost equals the mean for the wage. This motivates the insertion of a correction term relating wages to production values (LUAGE-LPPI-LPRO). It should also be noted that the low DW point to non-stationarity in some variables, particularly consumer prices.

°' There was a significant real wage fall as a result of a price surprise in 1987.
In the remaining sections of this paper, we will empirically test our hypotheses. This requires a measure of search costs from the perspective of the buyer for each transaction. As adeptly summarized in the quote above, this information is often missing, as is the case for our case study. To get around this constraint, the approach we adopt is to use a proxy, namely the distance of maize sellers to the marketplace. The further away a seller is from a market point where buyers and sellers congregate, the more difficult he or she is to find, causing buyers to incur higher search costs in transacting with them. Hence, the more remote a maize growing household is, the higher the search costs associated with their transactions and the lower the prices they receive for their maize.

The use of proxies to estimate search costs is common in the literature on this topic. In their study of small-scale farming households in South Africa Randela, Alemu & Groenewald (2008) use distance to markets as a proxy for search costs (amongst other variables) to identify factors that determine the extent of commercialization or market participation. Kuksov (2002) considers online marketplaces and the share of online sales as proxies for buyer and seller search costs and Benjamin & Lusht (1993) proxy the search costs associated with finding a rental apartment using the characteristics of the managing agent (e.g. whether they have a well-located rental office). Most studies (including this one) use proxies because of the dearth of data measuring specific transaction costs. Household budget surveys and agricultural censuses in particular do not tend to include a module directly measuring transaction costs, possibly because the large amount of detail that this would entail could make the survey unwieldy.

Given such data constraints, we have selected distance to market as a proxy for search cost because of its relevance to the marketing structure of Tanzania‟s maize market. The procurement of maize is a largely physical exercise that requires buyers to travel around villages visiting households, literally knocking on doors. The buyers travel mostly by bicycle (or sometimes on foot accompanied by a donkey), and some announce their arrival using a megaphone.

Using this proxy, the estimation challenge is to separate between straightforward marketing transaction costs, which are largely transport costs, and the costs relating to the search activity including search related transport. To do this, it helps to consider buyer transaction costs in two segments. The first is cross-country transport costs to the district or rural area where maize is produced. This segment represents the bulk of the buyer‟s marketing costs as shown in _table 1_ . Here, we expect search costs to be negligible as information about maize producing areas is 9
**Table 4.5b: Effectiveness of Bias Correction in Ethiopia HFPS by Urban-Rural domain**

||**ESS**<br>**Urban**|<br>|**Ethiopia - Urba**<br>**HFPS (n**<br>|**n**<br>**=2,270)**<br>||**ESS Rural**<br>**=3115**|<br>|**Ethiopia - Rur**<br>**HFPS (n**<br>|**al**<br>**=1,013)**<br>||
|---|---|---|---|---|---|---|---|---|---|---|
||**(n=3,655)**|_Adjust_|_ed Weights_<br>_†_|_Unadjus_|_ted Weights_<br>_†_|**(n,)**|_Adjust_|_ed Weights_<br>_†_|_Unadju_|_sted Weights_<br>_†_|
||_Mean_|_Mean_|_Difference_<br>_(2) - (1)_|_Mean_|_Difference_<br>_(4) - (1)_|_Mean_|_Mean_|_Difference_<br>_(7) - (6)_|_Mean_|_Difference_<br>_(9) - (6)_|
|**Characteristic**|_(1)_|_(2)_|_(3)_|_(4)_|_(5)_|_(6)_|_(7)_|_(8)_|_(9)_|_(10)_|
|Average household size|3.647|3.786|0.139|3.761|0.114|4.885|5.130|0.245|5.167|0.282*|
|Dependencyratio|0.651|0.653|0.002|0.626|-0.025|1.103|1.055|-0.049|1.041|-0.063|
|Female head(%)|0.346|0.343|-0.004|0.321|-0.026|0.223|0.192|-0.031|0.180|-0.043**|
|Age of head|38.728|38.993|0.265|38.590|-0.138|44.924|43.680|-1.243|43.365|-1.558|
|**_Religion of head_**|||||||||||
|Orthodox|0.574|0.577|0.003|0.587|0.013|0.431|0.447|0.016|0.447|0.015|
|Muslim|0.207|0.203|-0.004|0.194|-0.014|0.335|0.337|0.003|0.318|-0.017|
|Christian|0.213|0.215|0.002|0.215|0.002|0.210|0.204|-0.006|0.224|0.014|
|**_Marital status of head_**|||||||||||
|Married|0.618|0.631|0.013|0.644|0.026|0.798|0.814|0.016|0.819|0.021|
|Formerlymarried|0.220|0.222|0.002|0.205|-0.015|0.174|0.156|-0.017|0.141|-0.033*|
|Never married|0.162|0.146|-0.016|0.151|-0.011|0.029|0.030|0.001|0.040|0.012|
|**_Education level of head_**|||||||||||
|Head Literate|0.753|0.743|-0.010|0.813|0.06**|0.408|0.434|0.026|0.508|0.1***|
|None|0.287|0.308|0.021|0.225|-0.062**|0.637|0.613|-0.024|0.525|-0.112***|
|Primary|0.296|0.295|-0.001|0.299|0.003|0.296|0.297|0.001|0.340|0.044|
|Secondary|0.215|0.212|-0.003|0.247|0.031|0.047|0.056|0.008|0.081|0.033*|
|Tertiary|0.202|0.185|-0.017|0.230|0.027|0.020|0.035|0.014|0.055|0.034***|
|**_Working status of head_**|||||||||||
|Any|0.592|0.567|-0.025|0.601|0.010|0.804|0.827|0.022|0.827|0.022|
|Wage|0.302|0.283|-0.019|0.326|0.024|0.051|0.064|0.013|0.080|0.029*|
|Agriculture|0.124|0.131|0.007|0.104|-0.020|0.756|0.771|0.015|0.747|-0.009|
|Nonfarm enterprise|0.219|0.198|-0.021|0.215|-0.004|0.066|0.079|0.013|0.095|0.029|

†The results of an adjusted Wald test comparing weighted means are presented (*** p<0.01, ** p<0.05, * p<0.10).

38
**<u>Table 2: Anticipation of reform</u>**

|**Regime**|Statistic|Educational<br>level|**1**[Educ.,=<br>notNil]|**1**[Married =<br>Yes]|Age|
|---|---|---|---|---|---|
|Pre-reform|Mean|3.400|0.991|0.853|45.445|
||SD|(1.815)|(0.180)|(0.354)|(14.537)|
|Post-reform|Mean|3.010|0.986|0.4101|44.826|
||SD|(1.601)|(0.117)|(0.501)|(19.861)|
|P-value: Equal Means||0.999|0.142|<0.05|0.123|
|Density:_# of_<br>_Observations_||||||
|Pre-reform|4005|||||
|Pre-reform|3968|||||

_Notes_ : Table reports moments of the various observable household characteristics before and after the 2013 SIM <u>mandate; and the density of time variable which in this case is the number of observations across the two regimes.</u> The illustration in Table 2 partly supports the underlying argument. Changes in distributional moments of the various observable household characteristics before and after the 2013 SIM mandate are reported in Table 2. We expect to see significant changes in the relevant characteristics if households anticipated and reacted to the mandate before it came to effect. With the exception of the proportion of married respondents, the moment estimates in the table suggest no detectable evidence of reform anticipation as pre-reform moments are statistically similar to post-reform. Note that the analyses will directly control for all these observables to soak-up any potential adjustments to the reform. Thinking of time as a running variable, we would expect changes in the density of time if households significantly anticipated the unintended effects of the mandate (e.g., in the spirit of McCrary Test; McCrary 2008). We do not find evidence of this as the number of observations in the sample across the two regimes are similar. Significant differences in the number of observations before and after the 2013 mandate could have threaten the internal validity of the policy instrument and research design since the instrument interacts the change in policy with average mobile use activity.

# **4 RESULTS**

This section reports and discusses the main empirical estimates that quantify the sign and magnitude of business enterprises and poverty responses to changes in mobile use activity. We estimate our main Equation using OLS and 2SLS. β is our main parameter of interest. This captures the sign and size of the above outcome responses to the mobile infrastructure. While the ‐ 12 ‐