rafmacalaba/data-use-mentions-extended huggingface dataset:
Recall that we assume that the migrant first decides how much to send home, depending on his income and the income of his family remaining in the home country, and then decides how to send it. Aggregate remittances will therefore depend on wages in the host economy, income in the source economy, and the total number of migrants. In order to pinpoint informal remittances, we assume that high official costs in the form of the money transfer fee, the exchange rate spread, and the presence of a dual exchange rate affect primarily the extent to which remittances are transmitted formally. This allows us to estimate total remittance flows using the coefficients on these cost of transmission variables, assuming they take values such that individuals would always prefer formal transmission. This is explained in more detail in Section VI.

The model also highlights a testable feature of the informal sector. Informal transactions are likely to be smaller. The intuition is straightforward. If the fixed fee is high in the formal sector, then the fee as a fraction of the amount sent will be large if amounts are small and it will always be optimal to use the informal sector.

# **V.  The Data**

In order to estimate our model, we collected a panel of aggregate data on remittances from the IMF’s _Balance of Payments_ statistics. The dataset covers up to 104 countries for which workers’ remittances are reported over the 1995–2003 period. On average, we have five observations per country. As is standard practice, we define remittances as the sum of three items in the _Balance of Payments_ statistics: “Compensation of Employees,” “Workers’ Remittances,” and “Migrants’ Transfers.” Adjustments are however made for 11
WPS3617

# **Beyond Tariffs and Quotas: Why Don’t African Manufacturers Export More?**

George R.G. Clarke<sup>*</sup>

# World Bank Policy Research Working Paper 3617, June 2005

_The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the view of the World Bank, its Executive Directors, or the countries they represent. Policy Research Working Papers are available online at http://econ.worldbank.org._

> *  The data used in this paper are from the Investment Climate Surveys ©2002-4 The World Bank Group.  Responsibility for all errors, omissions, and opinions rests solely with the author. Senior Economist, Development Research Group – Competition Policy and Regulation, The World Bank, MSN MC3-300, 1818 H Street, NW, Washington, DC 20433.  Fax: 202-522-1155.  Tel: 202-473-7454.  E-mail: <u>gclarke@worldbank.org.</u>
17 defined as years from UC implementation, the VF variable is also be defined as years from VF implementation<sup>10</sup> . In practice, pinning down the date of VF implementation was not straightforward. We were able to obtain from the National Village and Urban Community Fund Office the date that each village registered with the Thai government. However, we could not identify the date that each village actually received its 1-million baht fund. What we do know is that, on average, villages received their money within 2-3 months of registration. We therefore assume that the “implementation” date of VF is 3 months after the registration date. We define the VF variable at the provincial level because we do not know the identity of the village in our LFS data; we define the VF variable as the proportion of villages in the province that had received the first tranche of VF money. The first fund was transferred in July 2001; by the end of 2002, about 73,941 villages (or 93.79 percent of all villages) received the money (Satsanguan 2006). Our VF variable – unlike the UC variable – exhibits variation within each of the blocks of provinces that comprise the four waves of the UC rollout; this extra geographic variation helps us separate the effects of UC from the effects of the VF program.

Table 3 shows the descriptive statistics of our dependent variables and covariates. The statistics are calculated from the total sample size of 4,770,735 individuals over the time period 1997-2005. For each variable, we report their population-weighted mean and standard deviation. As discussed earlier, the dependent variables include whether the individual is working, whether they work in the formal or informal sector, and which industrial sector they are in. About 67 percent of all Thai population age 15 and above

> 10 The value of this village fund variable would be equal to zero for municipal areas because villages are in non-municipal areas only.
by**|**sector**||||||||
|Manufacturing beverages|na|3.2|na|6.0||113||94|
|Food and beverage services|na|9.6|na|40.0||112||61|
|Retail trade|**19.6**|**9.6**|**36.0**|**10.0**|355|392|305|392|
|Transit services|48.0|na|42.0|na|81||108||
|**Average annual sales ('000 birr) b**|**y sector**||||||||
|Manufacturing beverages|na|7.5|na|12.2||113||94|

11
identify Brazilian firms for which environmental controversies have been recorded, and merge that information with bank loan data from their annual reports.

The key results of this paper are as follows. Brazilian banks have an outstanding credit exposure of BRL 811 billion to non-financial corporates that operate in sectors highly or very highly dependent on one or more ecosystem services. This amount represents 46 percent of the total non-financial corporate loan portfolio and 20 percent of the total credit portfolio, and is slightly tilted to firms that receive government-subsidized resources (so-called earmarked credit). The highest dependence is on the ecosystems that provide climate regulation, ground water and surface water. Based on historical sensitivity of Brazilian banks’ asset quality to macroeconomic conditions (see Vazquez, Tabak, and Souto 2012) and macroeconomic modeling of ecosystem services (World Bank, 2021), the GDP losses associated with the collapse in ecosystem services could translate into a cumulative long-term increase in corporate nonperforming loans (NPLs) in the order of 9 percentage points, other things being equal. Brazilian banks also have an outstanding loan exposure of BRL 254 billion or 15 percent of their corporate portfolio to firms potentially operating in protected areas. Such an exposure could increase to BRL 437 billion (25 percent of the corporate credit portfolio) should conservation gaps close, and to BRL 664 billion (38 percent of the portfolio) should all priority areas become protected.<sup>8</sup> Finally, for the 11 of 143 Brazilian listed firms for which environmental controversies have been recorded, as of December 31, 2019, banks had an outstanding loan exposure of BRL 109 billion (7 percent of the corporate credit portfolio).

To the best our knowledge, this paper is the first to attempt quantifying bank exposures to biodiversity loss in an emerging market and the second to do so in the relevant literature. The only paper we are aware of that explores biodiversity risks for the financial sector is the pioneering work by De Nederlandsche Bank <u>(DNB 2020), the Dutch central bank.
significantly – 50% from its peak (US$100/metric ton in 2018) – at the beginning of the pandemic. However, the price rebounded and continued to rise above its 2018 level, reaching US$160/metric ton. Coal prices were at their bottom when COVID cases, deaths, and stringency were at their highest in the first wave of COVID-19. The price then recovered and remained high during and even after the second wave of the pandemic. Again, visual inspection suggests that the price of coal responds to the stringency of public health measures. The story is somewhat different for the price of natural gas, whose path in the United States seems to have diverged from that in Europe and does not necessarily co-vary with COVID-19 cases or stringency.

# **3. Methods**

Our first goal is to establish whether COVID-19 severity affected total electricity generation and, if so, by how much. We take advantage of our panel dataset, which covers selected countries for two years before and almost two years into the pandemic, and fit the regression: i 1C C i 1 i 3 i 4<sup>C</sup> i i i i i i i (1) EE = ββ CC + ββ CC + ββ HHC<sup>+ ββCC+ ααHH+ δδ+ θθ</sup> + ηη + εε where _i_ denotes the country, _t_ the date, _COVID_ measures COVID severity, _C_ is generation capacity, _HDD_ and _CDD_ are the heating and cooling degree days, respectively, and _H_ is a holiday dummy.

Equation (1) contains a rich set of fixed effects (country-by-year, country-by-month, and country-by-day-of-the-week). It controls for installed capacity in an effort to capture the underlying generation patterns. We note, however, that daily data capacity has only very limited variation over time, and thus it tends to act almost like a country fixed effect. The interpretation of Equation (1) is straightforward: Essentially, we wish to see whether COVID-19
least one vaccination by 0.076 to 0.118 (triple-interaction coefficients in column (6) of Table 4. The average number of vaccinations (conditional on receiving at least one vaccination) for girls preceded by a firstborn girl during the early diffusion period is 6.64 in NFHS data. Thus the estimated effects for at least one vaccination translate into an average increase in the number of vaccinations of 0.505 (6.64 * 0.076 = 0.505) to 0.784 (6.64 * 0.118 = 0.784). Oster (2009) suggests that each vaccination reduces mortality during ages 1 to 4 by 0.26 p.p.. Thus the implied effect on EFM through vaccination is 0.131 p.p. (0.26 * 0.505 = 0.131) to 0.204 p.p. (0.26 * 0.784 = 0.204), which translates into 7 percent (0.131/1.996 = 0.066) to 10 percent (0.204/1.996 = 0.102) of the decline in EFM.

Note that the mortality measure is 12-36 months in Jayachandran and Kuziemko (2011) and is 1-4 years in Oster (2009). However, any exogenous change in these mortality measures would generate an almost one-to-one change in the mortality measure we use, i.e., death before age five.

> 62We assume that the share of children who are being breastfed and the mortality rate during 12-24 months are the same as those for 12-36 months used in Jayachandran and Kuziemko (2011).

> 63 Solving 0 _._ 481 _x_ + 2(1 _−_ 0 _._ 481) _x_ = 2 _._ 05 yields _x_ = 1 _._ 35, where 0.481 is the fraction of children aged 12 to 36 months that are being breastfed in the sample analyzed by Jayachandran and Kuziemko (
to control for the technological heterogeneity of firms (as they respond to purely crosssectional variation in business environment). The relationship between business environment and productivity that we map out in this way is a short run effect as it is conditioned on the current (or observed) spatial distribution of plants.

Profit maximizing firms would tolerate regional gaps in business environment as long as these are compensated by mobility or relocation costs, or by other sources of productivity in the current location-notably, natural geography, market access and agglomeration economies. In other words, if any two locations differed only with respect to business environment (and there were no mobility costs), all plants would eventually have (re)located away from regions of poorer business environment. This means that there would always be a “reallocation of plants” between cities and regions over any period of time in response to persistence differences in business environment.<sup>9</sup> The estimates of the effect of business environment on local or regional industrial productivity we report here are short run effects as they omit (the productivity effects) of the spatial reallocation of activities.

On the other hand, being based on longitudinal analyses of aggregate (state level) data, the productivity gaps that Besley and Burgess (2004) attribute to differences in business environment are of a long run nature as they include spatial reallocation effects (as well as the short run effects). There is, however, the downside to the use of aggregate data in this context in that we cannot separately identify short run effects from aggregate data. We think that such identification is important because firms base their location choices and investment decisions on short-run productivity premiums or shortfalls, rather than on their long-run counterparts. . We also believe that the only practical way we can achieve this identification is probably estimating the effects of business environment at the plant level. At the same time, it is the long run productivity effects that would measure the true cost of possible deficiencies in a location’s business environment
geographical levels.

In this paper, I estimate intergenerational mobility in education for LAC countries at a disaggregated regional level using data from 91 censuses. The analysis covers 24 countries spanning more than half a century (between 1960 and 2012). I rely on samples of co-residents (i.e., children living with their parents or older relatives). To minimize the impact of coresidence, I investigate mobility in education at the bottom of the educational attainment distribution by focusing on primary education, which can be measured with a high degree of confidence between ages 14 and 18. Furthermore, an important share of the population does not attain more than primary education in the period analyzed and this focus allows me to create indicators that are directly comparable to the estimates recently generated for 27 countries in Africa (see Alesina, Hohmann, Michalopoulos, & Papaioannou, 2021), a continent that shares the feature of having high levels of income inequality despite its lower levels of income and higher poverty rates.

The estimates of upward (and downward) mobility measured as the likelihood of finishing (or failing to finish) primary education, conditional on having parents who failed to finish (or who were able to finish) primary school, show wide cross-country and within-country heterogeneity. In LAC, the distance between the most and least upwardly mobile countries is similar to what has been recently documented in Africa, although the least mobile countries in Africa are less mobile than the least mobile country in LAC. I find only small differences by gender, but I do document a declining trend in the mobility gap between urban and rural populations. At the sub-national level, there is heterogeneity in mobility across districts/provinces, and some countries show lower levels of mobility in the northern regions (e.g., Brazil), whereas the opposite is true for Mexico. However, the variability is much lower in countries with lower number of regions and less population. The level of mobility at the sub-national level is highly positively correlated to the share of primary
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sample.<sup>12</sup> Second, there is no significant difference between response rates of treatment and control groups. Some of the final interviews could not be conducted face-to-face and we investigate whether the likelihood of face-to-face interview is correlated with treatment status, and reassuringly it is not (column 2). Nevertheless, we control for mode of interview in all subsequent analysis.

Finally, the take-up within both treatment and control groups was very high. Out of the sample of individuals assigned to either group, 96% reported watching their assigned soap during the study period, and there was no variation across treatment and control groups. Furthermore, Table 3 investigates whether there was substantial crossover or treatment contamination, with the control group also watching the treated show, Scandal. In either follow-up 1 or 2, we find that less than 12% of Muvhango viewers claim to have also watched Scandal in the last four weeks, and a third of these viewers watched several other shows too. The tabulations show that 2% of respondents watched Scandal and another show, about 1% watched two other shows, and 0.5% watched three or more other shows. A large proportion – 38% in follow-up 1 and 29% in follow-up 2 watched entirely other shows and did not watch Scandal. While these are reassuring findings, we note that such crossovers will only underestimate treatment effects in our subsequent analysis.

# **6. Results and Discussion**

This section presents the main analysis on financial knowledge and behavior. Since our research methodology uses random assignment, we compare the cross-sectional averages between the treatment and control groups in a regression framework, and conclude that any difference between the two groups is due to viewing the financial messages in Scandal. Additionally, we control for mode of interview and use robust standard errors.

Note that while the two intermediate CATI surveys provide insight into the immediate effects of our intervention, the outcomes measured in these surveys are not directly comparable with the outcomes in the final face-to-face survey
countries in all variables except in financial conditions, short-term interest rates, business confidence, policy uncertainty, and policy interest rates (at least 4 countries, because of more limited data availability in the original series). The sample coverage mentioned in the table is the maximum number of countries and the sample size varies by year or quarter. Figures A2.1 to A2.4 display time series data of global aggregate. Output from other data sources is also utilized for comparison purposes: the IMF World Economic Outlook (October 2019) has annual data available since 1980 and the United Nations National Accounts Main Aggregates Database has annual data starting in 1970.

65
# **Table A8. Descriptive Statistics for Programs in Brazil**

## **_Using Program-Level Data from the WBSCPS and Administrative Sources_**

|**Variable**|**Progr**<br>**matc**<br>**indivi**<br>**Mean**<br>**(1)**|**ams not**<br>**hed with**<br>**dual data**<br>**Std.Dev.**<br>**(2)**|**Program**<br>**with in**<br>**d**<br>**Mean**<br>**(3)**|**s matched**<br>**dividual**<br>**ata**<br>**Std.Dev.**<br>**(4)**|**P-value**<br>**diff.**<br>**(1) – (3)**<br>**(5)**|
|---|---|---|---|---|---|
|**Panel A. Programquality determinants**||||||
|_Infrastructure_||||||
|Program offers at least one online class|0.34|0.47|0.33|0.47|0.74|
|>30% classes can be taken online|0.13|0.34|0.10|0.30|0.19|
|Number of workshops or labs available for practice|4.57|4.09|5.72|5.61|**0.
global greenhouse gas emissions (Baccini _et al._ , 2012).

To measure the impact of forest loss arising from RTAs, we utilize the Global Forest Change dataset by Hansen _et al._ (2013). These data provide high resolution estimates of year 2000 forest cover and annual estimates of forest loss for the entire terrestrial surface of the earth. Following Abman and Lundberg (2020) and Leblois _et al._ (2017) (among many others), we aggregate these

> 5See Monteiro (2016) for details.

8
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population density and adequate transport facilities to make rural services accessible to the villages and so may be less applicable to large parts of Sub-Saharan Africa. We hypothesize that the absence of relatively cheap, labor-intensive goods and services in rural areas will result in a slower shift of demand from foods to services in Sub-Saharan Africa than in Asia, with consequent weaker demand linkages to the rural nonfarm economy.

Of the few household expenditure studies which allow assessment of African rural consumption linkages, the most comparable were uiadertaken for farm households in Gusau, Northern Nigeria (Hazell and Roell, 1983), rural households in Sierra Leone (King and Byerlee, 1977), and households in three villages in Zaria Province, Northern Nigeria (Simmons, 1976b). These are suumarized in Table 9 together with comparable results for farm households from two Asian studies: the Mud& region of Malaysia (Hazoll and Roell, 1983) and North Arcot district, South India (Hazell and Ramasamy, forthcoming).

As the data in Table 9 indicate, African spending patterns support far less rural nonfarm activity than do those in Asia. Average expenditure on rurally produced nonfoods averages about 18 percent in Muda and North Arcot, double the roughly nine percent prevailing in Gusau and Sierra Leone. And with the marginal budget shares, crucial predictors of the linkages to be anticipated from growing incomes, the gap widens. African consumers in Gusau and Sierra Leone spend only 11 to 12 percent of incremental income on rurally-produced nonfoods, while the comparable Asian figures from M uda and Gusau stand at 31 to 26 percent, triple those in Africa. In part, this difference arises because African consumers spend far more of their average and marginal income on rurally-produced foods. While total rural consumption linkages (on foods plus non-foods) are approximately equal in the cases reviewed, the Asia data indicate greater diversity into nonfoods.
Pr( _sfpdt_ = 1) = _φ_ ( **x** _fpdtβ_ + _δi_ + _δcd_ + _δt_ + _ufpdt_ ) (2) where _φ_ is the probit function and _ufpdt_ is an error term. Our specification includes industry fixed effects at HS2 ( _δi_ ), origin-destination fixed effects ( _δcd_ ), and spell-start year fixed effects ( _δt_ ). The vector of regressors **x** _fpdt_ includes measures of the firm’s scale and scope as well as proxies for agglomeration and market attractiveness. These proxies are counts of (i) _n_<sup>_c_</sup> _pdt_<sup>,thenumber</sup> of firms from origin country _c_ exporting product _p_ to destination _d_ ; (ii) _nfpt_ , the number of destinations to which firm _f_ exports product _p_ ; (iii) _nfdt_ , the number of products that firm _f_ exports to destination _d_ ; (iv) _n_<sup>_c_</sup> _dt_<sup>,thenum-</sup> ber of (product _×_ firm) combinations active in the bilateral trade between origin _c_ and destination _d_ ; they also include (v) _vfpdt_ , the initial value of firm _f_ ’s export spell (product _p_ to destination _d_ ); and (vi) _zfp_ , the share of product _p_ in firm _f_ ’s overall export sales. That is, the notation convention is to omit the index of the dimension over which the count is summed. All counts are put in logs, and we use robust standard errors clustered at the product-destination level throughout.

In customs data, E.U. countries are entered as separate destinations rather than as a whole. We have kept this convention, so a destination should be taken, as far as the E.U. is concerned, as a member state. This creates an asymmetry in the treatment of destinations between the U.S., which is taken as a whole, and the E.U., which