rafmacalaba/datause-encoder-data huggingface dataset:
7 dealt with **here** are trade misinvoicing and capital gains derived from crosscurr-ncy fluctuations. Although data on trade misinvoicing was available coverage was incomplete and some numbers appeared doubtful. On tLe other hand, capital gains/losses from cross-currency fluctuations could only have been calculated fce toreign debt as the currency composition of private foreign **assets** Ls unknown.

# i) Income from Poreign Assets.

Income from private foreign assets requires knowledge of the stock of wealth held by domestic residents abroad. A direct measurement of this stock **is** unavailable except for deposits of Mexicans in foreign banks. This is clearly incomplete as it does not measure bond holdings, equity and real estate assets held by Mexicans abroad. Neither does it measure Mexican's bank deposits abroad held by off-shore companies. To remedy this problem we propose to use an indirect estimate of the stock of foreign assets hold by Mexicans obtained by Brideau, Eggerstedt and van Wijnbergen (1991). aw private capital outflows were derived residually as the difference between, on the one hand, the sum of external debt and DFI flows, and on the other hand, the sum of the current account deficit (excluding interest retained !broad), the increase in net reserves and the increase in other public foreign assets. This flow measure was completed by incorporating an unofficial estimate of additional worker's remittances (compared to the official figure) before 1988. The total private capital outflow was then estimatad by adding the new flow adjusted for worker's remittances to reinvested income from foreign assets. It was assumed that 100% of the income was reinvested and that the rate of return was explained two-thirds by the US CD rate and one-third by the threemonth LIBOR rate. The stock, in turn, can be obtained by adding tRe total flow to the stock of the previous period.

# ii) Worker's Remittances.

In late 1990 the government revised the az+-hodology to estimate annual worker's remittances. The new estimate, which implied an upwards revision of about US$ 1.5 billion, was only reported for 1989 and 1990. Thus, it is likely that worker's remittances prior to 1989 are underestimated. If this is the case, the current account deficit would be overestimated and capital flight underestimated. Preliminary and yet unofficial estimates of worker's remittances reported in Table 1 were used to adjust the current account balance.

Taile 1. Wo,:.terls Remittances Adjustment.

|Year|Official|Adjusted|Change|
|---|---|---|---|
|1980|140|569|429|
|1981|128|692|564|
|1982|98|690|591|
|1983|111|824|712|
|1984|176|943|767|
|1985|173|971|797|
|1986|180|.082|901|
|1987|207|1237|1030|
|1988|209|1526|1316|
The results from the cross-randomized public and private raffle treatments are inconclusive. Effects of either type of raffle are mostly not statistically significantly different from zero, and the few statistically significant coefficients are inconsistently signed across regressions. For this reason we focus this paper’s attention on interpreting the effects of the “no raffle” savings treatments.

This paper contributes to the burgeoning literature on the effects of formal savings accounts and in this sense is related to the field experiments of Dupas and Robinson (2010) and Atkinson et al. (2010). Dupas and Robinson (2010) offer ordinary savings accounts with de facto negative interest rates to Kenyan urban entrepreneurs, finding positive impacts on investment and income for women. In this paper, by contrast, we explicitly test whether impacts of commitment savings offers are larger than impacts of ordinary savings offers. We also use a very different sample, (mostly) male farmers in rural Malawi. Atkinson et al. (2010) offer microcredit borrowers in Guatemala savings accounts with different features, including reminders about a monthly commitment to save and a default of 10% of loan repayment as a suggested monthly savings target. They find that both features increase savings balances substantially. However, they use administrative records from the lender which restricts the number of observable outcomes and limits analysis of the mechanisms that lead to changes in savings behavior. Our paper is also related to Dupas and Robinson (2011) in seeking to understand the relative importance of various barriers to savings. Dupas and Robinson (2011) do so in the context of ROSCAs, while we provide formal savings facilities.

The remainder of this paper is organized as follows. Section 2 explains the study design and briefly describes the characteristics of the sample. Section 3 explains the estimation strategy. Section 4 presents the main empirical results. Section 5 discusses heterogeneous effects and the mechanisms through which savings accounts may have affected savings and other outcomes. Section 6 concludes.

# **2.** **<u>Experimental design and survey data</u>**

The experiment was a collaborative effort of Opportunity International Bank of Malawi (OIBM), Alliance One, Limbe Leaf, the University of Michigan and the World Bank. Opportunity International is a private microfinance institution operating in 24 countries that offers savings and credit products. Alliance One and Limbe Leaf are two large private agribusiness companies that offer extension services and high-quality inputs to smallholder farmers 5
# **4 Experiment One**

## **4.1 Experiment Design**

This study took place among property owners in Congo Town, one of the tax zones in Monrovia, the capital city of Liberia. This area was identified as having many properties that could be brought into the tax net.

The first activity was creating a property database. From April to June 2014, I worked closely with the LRA to conduct a “block mapping” project to collect information on property locations and features. Enrollment agents (short-term government contractors) went doorto-door in teams of two to raise awareness of the real estate tax using brochures and flyers. They also completed a brief survey with residents, using mobile devices to obtain information about each property and its owner. The data collected in this enumeration process resulted in an electronic property database for taxation. This was the first time the government had electronic records and digital photographs of these properties.<sup>14</sup> High-value properties, such as hotels, banks, and other commercial properties, were excluded from the enumeration list because the LRA did not want to include them in the experiment, given their revenue potential. In addition, 5 percent of the enumerated properties were found to be on the tax roll already and were thus removed from the experiment sample. In all, 571 properties belonging to 464 owners made up the sample.

Properties in the sample were randomly assigned to four groups. The control group received a generic notice that informed property owners of their responsibility to pay the real estate tax and gave instructions about how to comply. The notice did not contain any information specific to the property owner but was simply addressed “Dear Property Owners.” The notice for the first treatment group (the _identification and penalty notice_ ) contained the same information about how to comply; however, it was personalized by including the owner’s name and a photograph of the property (obtained during the door-to-door enumeration). It also included the legal penalties for noncompliance, citing relevant sections of the Liberia Revenue Code. The notice for the second treatment group (the _identification no-_

> 14 Following this initial phase, the government extended data collection to over 40,000 properties across Monrovia a few years later.

12
**Table 12:** Job Flows - A Baseline Difference-in-Difference Analysis

||**1990s**|||**1990s, transition late **|**1990s**|
|---|---|---|---|---|---|
||(1)|(2)|(3)|(4)<br>(5)|(6)|
|Constant|-0.0348<sup>_∗∗∗_</sup>|0.0004|0.0524<sup>_∗∗∗_</sup>|0.1153<sup>_∗∗∗_</sup><br>0.1376<sup>_∗∗∗_</sup>|0.1810<sup>_∗∗∗_</sup>|
||[0.0100]|[0.0118]|[0.0118]|[0.0095]<br>[0.0109]|[0.0107]|
|USA SUM|0.7097<sup>_∗∗∗_</sup><br>[0.0183]|||0.6621<sup>_∗∗∗_</sup><br>[0.0173]||
|USA SUM <sup>_∗_</sup>EU||0.5860<sup>_∗∗∗_</sup><br>[0.0288]||0.5746<sup>_∗∗∗_</sup><br>[0.0274]||
|USA SUM <sup>_∗_</sup>Transition||0.8282<sup>_∗∗∗_</sup><br>[0.0325]||0.6878<sup>_∗∗∗_</sup><br>[0.0308]||
|USA SUM <sup>_∗_</sup>LAC||0.7493<sup>_∗∗∗_</sup><br>[0.0329]||0.7493<sup>_∗∗∗_</sup><br>[0.0312]||
|USA SUM <sup>_∗_</sup>_<_20 Workers|||0.5628<sup>_∗∗∗_</sup><br>[0.0227]||0.5385<sup>_∗∗∗_</sup><br>[0.0215]|
|USA SUM <sup>_∗_</sup>20-49 Workers|||0.3975<sup>_∗∗∗_</sup><br>[0.0317]||0.3875<sup>_∗∗∗_</sup><br>[0.0301]|
|USA SUM <sup>_∗_</sup>50-99 Workers|||0.3157<sup>_∗∗∗_</sup><br>[0.0351]||0.3169<sup>_∗∗∗_</sup><br>[0.0333]|
|USA SUM <sup>_∗_</sup>100+ Workers|||0.1764<sup>_∗∗∗_</sup><br>[0.0566]||0.2090<sup>_∗∗∗_</sup><br>[0.0537]|
|Observations|935|935|935|940<br>940|940|
|Adjusted R-squared|0.69|0.70|0.74|0.69<br>0.69|0.73|
|Standard errors in brackets.<br>include country dummies. U<br>OECD European countries. <br>the countries in Latin Amer|<sup>_∗_</sup>signifcant<br>SA SUM: in<br> Transition d<br>ica.|at 10%, <sup>_∗∗_</sup><br>dustry/size<br>enotes the|signifcant a<br> job realloc<br>countries in|t 5%, <sup>_∗∗∗_</sup>signifcant at 1%.<br>ation in the United States. <br> Central and Eastern Europ|All regressions<br> EU denotes the<br>e. LAC denotes|

Source: Own calculations based on harmonized firm-level database.
**_Table 10: Poverty convergence regressions_**

||(1)|(2)|
|---|---|---|
|Dependent variable:|||
|Growth of percentage of population living in poverty ov|er a decade||
|Log initial poverty level|0.072**|0.052|
||(0.034)|(0.079)|
|VA per worker: Annualized gr. rate||0.108|
|||(2.550)|
|Log initial poverty level x VA per worker: Ann. gr.|||
|rate||1.075|
|||(4.227)|
|Constant|‐0.043*|‐0.078|
||(0.022)|(0.049)|
|Observations|24|24|
|R‐squared|0.167|0.245|
|Stardard errors in parenthesis.|||
|*** p<0.01, ** p<0.05, * p<0.1|||

A more likely reason for the persistence of the poverty gap between regions is related to the fact that not all industries are converging in labor productivity. It is possible that industries converging in labor productivity are less relevant to poverty reduction because they employ fewer low skilled workers, have weaker supply chain linkages to industries likely to employ low‐skilled workers, and/or are less likely to produce goods that have a large share in the consumption basket of the poor. This would be in line with the findings of Loayza and Raddatz (2010) who argue that the composition of growth matters for poverty reduction. Their evidence suggests that growth coming from labor‐intensive sectors (such as agriculture, construction, and manufacturing) is most supportive of poverty reduction. Hence, it could be that the relatively weak productivity convergence in agriculture and services is hindering poverty convergence.

# **5. Are workers moving into sectors that are catching up in labor productivity?**

The impact of convergence in select sectors on convergence in overall labor productivity and poverty could, in potential, be higher if those sectors account for a growing share of employment. However, sectorial employment shares are shifting slowly, and not in a direction that particularly favors converging sectors. As seen in Figure 7, the tertiary sector – within which labor productivity has not been converging – as increased its share of total employment from around 52% to 58% between 2002 and 2012. The sector showing the most robust convergence – the secondary sector – has increased its share by a smaller amount, and it continues to have a small share of total employment (up from 14% to 17%). Meanwhile, the primary sector – another sector where there is convergence, especially in mining – has reduced its share in employment, offsetting the effect of the small rise in the secondary sector’s share.

20
correlation between internet access and an indicator of inequality in income distribution such as the Gini coefficient.

**Figure 3. A naive correlation between internet use and income distribution**

<!-- Start of picture text --> .~8<br>y = -. 0999x + 6.9979<br>u0 6 R'= 0.1356<br>4<br>0.<br>E<br>r 0<br>0 10 20 30 40 50 60 70<br>GIN Coefficient<br><!-- End of picture text --> Overall, these stylized facts are a first attempt to qualify the more blurred notion of a digital divide. Income is what matters most. A richer country is expected to have more internet users. Perhaps a more subtle result is that, for a given level of average income, an additional dollar given to the poor more than compensates for the diminished internet use made by the rich from whom a dollar is taken away, resulting in an overall increase in internet access.

# 3.2. A **more formal look at the facts**

In the remaining part of this section, we conduct a multivariate analysis to investigate if these findings still emerge after a closer scrutiny, once additional factors are also taken into consideration. We are also interested in trying to track down the relevance of policy variables. We estimate a simple regression building on the naive correlations just discussed as well as on additional information on internet access costs and on access to complementary equipment (e.g. computers) as determinants of growth in internet access and use. While the naive correlations in the preceding section exploit the cross country differences in internet diffusion at one point of time, in the rest of the analysis we use longitudinal data which allows to control for country (and, at times, continent) fixed effects which are potentially correlated with the dependent variables and might lead to biased estimates of the effect of technology and growth on internet diffusion. By allowing for country specific fixed effects we attempt to purge our estimates of the effect of unobserved differences in internet diffusion across 9
characteristics, which helps mitigate against the concern that our results are potentially biased by the non‐random assignment of interviewers to respondents.

# **4. Discussion**

Our findings illustrate that interviewer characteristics can impact survey data. A methodological implication is that researchers may wish to randomly assign enumerators to respondents, or at a minimum control for interviewer fixed effects in regression analysis of survey data. A substantive implication is that, to the extent that the social interaction during a survey interview echoes social interactions in the real world, our results can offer insights into the psychological mechanisms through which vulnerable adolescent girls perceive others and strategically attempt to manage how they are perceived.

# **References**

- [1] <mark>DUFLO.E, P.DUPAS AND M.KREMER (2015). “Education, HIV, and Early Fertility: Experimental Evidence from Kenya.”</mark> _<mark>American Economic Review</mark>_ <mark>,</mark> _<mark>105</mark>_ <mark>(9): 2757‐97.</mark>

- [2] HAMERMESH.D.S. AND J.E.BIDDLE (1994). “Beauty and the Labor Market.” _American Economic Review_ , _84_ (5): 1174‐94.

- [3] LANGLOIS.J.H., L.KALAKANIS, A.J.RUBENSTEIN, A.LARSON, M.HALLAM AND M.SMOOT (2000). “Maxims or Myths of Beauty? A Meta‐Analytic and Theoretical Review.” _Psychological Bulletin_ , _126_ (3): 390‐423.

- [4] TOURANGEAU.R AND T.YANG (2007). “Sensitive Questions in Surveys.” _Psychological Bulletin_ , _133_ (5): 859‐883.

- [5] WEST.B.T AND A.G.BLOM (2017). “Explaining Interviewer Effects: A Research Synthesis.” _Journal of Survey Statistics and Methodology_ , _5_ (2): 175‐211.

6
respectively. The post-Covid-19 interview sample was 17,480 individuals belonging to 3,414 households but presented a similar regional distribution as the pre-Covid-19 sample.

Our identification strategy to assess the impact of the national lockdown measure on household welfare explores the proactive measure of the Government of Comoros’s lockdown policy that came into effect on March 23, 2020 (see Figure 1). Our evaluation uses as a treatment variable a dummy that takes the value 1 if a household was surveyed after March 23, 2020 and 0 otherwise.

In validating our treatment effect, it is worth noting that the Covid-19 effect could come from the direct contagion of the virus or through the curtailment measures implemented by the national government. First, on the effect of contagion, we do not know from the survey whether individuals suffered from Covid-19, and thus this cannot be estimated in our analysis. Nevertheless, the Comoros was one of the last countries with lowest records of infection from the virus.<sup>6</sup> According to the World Health Organization’s recorded Covid-19 cases, the Comoros accounted for 4,038 of the 207 million worldwide cases of Covid-19 by August 15, 2021. The number of confirmed cases in the Comoros was only 0.46% of the country’s population. Second, curtailment measures are expected to have restricted and distorted socio-economic activities and markets. Hence, our treatment indicator using the dummy variable of national lockdown is a good approximation of the impact of Covid-19 curtailment measures on household welfare. It is acknowledged that the knowledge of Covid-19 was already in circulation after the President of the Comoros addressed the nation on March 16, 2020. Therefore, we may have reason to believe there may be anticipatory effects as people changed their behavior in response to the news. As such, we test the sensitivity of our analysis using the date the president addressed the nation as an alternative treatment cutoff.

> 6 Comoros and Lesotho were the two countries in Africa that were still virus-free (Lone and Ahmad, 2020) by April 2020 a month after the WHO announced the virus a pandemic.

12
Excluding the rural population: the impact of public expenditure on child malnutrition in Peru

# _Gissele Gajate-Garrido_<sup>∗</sup>

**JEL classification:** D13; H51; I12; J13

**Sector board:** Health, Nutrition and Population (HNP)

**Keywords:** Child; Nutrition; Public spending; Urban; Rural

> ∗ Gissele Gajate-Garrido (corresponding author) is a Research Fellow at the International Food Policy Research Institute (IFPRI); her email address is g.gajategarrido@cgiar.org. The author thanks Dora L. Costa, Pascaline Dupas, John Hoddinott, Naomi Lamoreaux, Arleen Leibowitz, Marc Luppino, the anonymous referees from the World Bank Economic Review, and participants in the UCLA applied micro seminars for thoughtful comments and suggestions. She is also grateful to Javier Escobal and Monica Lizama for providing her with access to the Young Lives survey data and to Milagros Villagarcia and Julio Mejia for providing public expenditure data. The data used in this study come from Young Lives, a 15-year survey investigating the changing nature of childhood poverty in Ethiopia, India (Andhra Pradesh), Peru, and Vietnam (www.younglives.org.uk). Young Lives is core-funded by UK aid from the Department for International Development (DFID) and co-funded from 2010 to 2014 by the Netherlands Ministry of Foreign Affairs. The views expressed here are those of the author. They are not necessarily those of Young Lives, the University of Oxford, DFID, or other funders. The usual disclaimers apply.
||Asia/|Latin America/||
|---|---|---|---|
|Management|Pacific|Caribbean|Africa|
|National Ministry|-0.114|0.012|-0.203|
||(1.32)|(0.13)|(1.59)|
|Sub-National Ministry|0.523|0.055|-1.735|
||(5.62)**|(0.54)|(1.58)|
|Delegated by Government||-0.825|0.458|
|||(1.17)|(0.63)|
|Collaborative|-1.745|0.126|-1.432|
||(1.86)|(0.29)|(1.85)|
|Joint|0.108|0.696||
||(0.11)|(1.78)||
|Private Governance||0.327|-0.369|
|||(0.91)|(0.27)|
|Individual Landowners|-0.899|0.111||
||(1.52)|(0.25)||
|Non-Profit Organizations||-0.103<br>(0.20)||
|For-Profit Organizations||0.261<br>(0.51)||
|Indigenous Peoples|0.678|0.372||
||(2.70)**|(4.18)**||
|Local Communities||0.152|0.293|
|||(0.71)|(0.69)|
|Park Status||||
|Designated|1.455|-0.225|0.106|
||(1.44)|(1.48)|(0.40)|
|Inscribed|1.536|0.227|-0.480|
||(1.47)|(0.55)|(1.00)|
|Proposed|1.485|-0.625|0.170|
||(1.47)|(3.41)**|(0.65)|
|Constant|-0.840|0.883|0.380|
||(0.83)|(5.03)**|(1.24)|
|R<sup>2</sup>|0.06|0.05|0.07|
|Observations|14,761|20,328|7,875|
|Number of Parks|1,359|1,887|729|

Absolute value of z statistics in parentheses * significant at 5%; ** significant at 1% 13
The analysis focuses on the price effects of maize, rice and cassava, which form the main staple and constitute on average more than 30% of the food budget share. We find evidence for a large net negative welfare effect of price rise in rural areas, and a small, negative effect in the urban areas. Overall, the simulations show that a 10% increase in maize prices would result in an average household welfare (as measured by consumption per capita) reduction of 1.2% in the rural areas and 0.2% in urban areas. The welfare reductions due to a similar increase in the price of rice and cassava are much smaller – 0.2% and 0.4% respectively in rural areas, and 0.2% and 0.1% respectively in the urban areas. The largest negative welfare impacts are seen in poorer provinces where the dependence on maize for food consumption is higher. These include Manica, Niassa and Tete where a 10% price increase would result in a negative welfare impact of more than 2.5% on average in the rural areas.

These effects are higher when we take into consideration the observed price rise during 2016, which was larger than 10%. The price of maize (relative to the consumer price index for food items) increased by as much as 89% between 2014 (at the start of the household survey sample period) and 2016. Prices of rice and cassava also increased, albeit at a relatively lower level of 22% and 37%, respectively. The net welfare impact of these price increases ranges from a loss of 11.7% in rural areas to 2.7% in urban areas with respect to initial household expenditure. The negative effect is much higher (greater than 20%) in the rural areas of Niassa, Tete, Manica and Sofala.

The negative welfare effect translates into an increase in poverty. Overall, the 2016 food price spike led to an increase in the poverty headcount ratio of 5.9 percentage points. The bulk of the poverty increase occurred in the rural areas, with the provinces of Tete and Manica bearing much of the brunt. We also examine the sensitivity of these estimates to model assumptions – in particular, assumptions about how much of the increase in consumer prices is transmitted to producer prices. We simulate the poverty estimates under various scenarios and find that under the assumption of no change in producer prices, the poverty headcount ratio increased by close to 8 percentage points. This corresponds to an upper-bound on the potential poverty impact of the price rise – this is also because the simulation does not account for behavioral responses such as substitution of crops produced and food consumed. At 3.5 percentage points, the negative effects 3