rafmacalaba/datause-encoder-data huggingface dataset:
If market failures are not associated with imitation, then the second _α_ in equation (1) would not have an effect on _D_ , and barriers would have an unambiguously negative correlation with discovery. Also, the absence of market failures associated with imitation would imply that the effect of an increase in returns to discovery is not affected by barriers to entry.

If imitators can benefit from spillovers emanating from the original discovery, we would observe an ambiguous relationship between discovery and barriers to entry. Furthermore, we would expect that the relationship between returns to discovery and the frequency of discovery would be affected by variations in barriers to entry. The effect of higher returns on export discoveries would be _greater_ in countries with _higher_ barriers to entry, as first movers would be able to appropriate a larger share of the export returns. That is, in this scenario pioneers would have a greater incentive to experiment for a given level of expected returns. Conversely, if barriers to entry are low, then an increase in exogenous returns to exporting will have a smaller effect on discovery, as much of those returns will leak to imitators. This, then, is our test of the market failure hypothesis: how does the relationship between exogenous returns to discovery and the frequency of observed discovery vary with barriers to entry.

# **3. Data and Methodology**

To test this hypothesis, we require a metric of inside-the-frontier innovation (when a good enters a country’s productive basket for the first time), which has not yet been developed. Production data highly disaggregated at the product level would be the ideal source of such a metric, but are unavailable for most countries. As such, we exploit export data, which for reasons of customs reporting are available for a broad crosssection of countries at a high level of disaggregation by product.

The problem with using export data seems obvious: a product emerging as a new export may have been produced domestically for some time, and therefore would not represent a true inside-the-frontier innovation. However, exporting a particular good for the first time, even if it was already produced domestically, is itself an entrepreneurial act that requires discovery and can be imitated (Ibeh 2003). In other words, the act of exporting is itself a discovery worth investigating. Furthermore, the increasing importance of trade and foreign markets for developing countries, most of which are pursuing an export-led development strategy, means that discovering new products is primarily a search for new exports.

Worldwide export data are drawn from the United Nations COMTRADE database under the Harmonized Commodity Description and Coding System (HS), available beginning in the early 1990s for most countries at the 6-digit level of disaggregation (approximately 5000 products). These data have been used widely to analyze export dynamism and growth, as well as geographic patterns in export growth, but until now have not been used to study the emergence of new exports.

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What are the ways in which the activities of informal, local legal institutions might reduce inequality and poverty? To begin with, it is clear that local legal institutions are rarely insulated from other forms of government and social power (Characteristic 3). As a result, informal negotiations under the auspices of local legal institutions are dominated by elites, and weaker parties typically settle for whatever meager justice the powerful offer. A study of 18 villages in Indonesia found that “in all cases where [such] power imbalances existed, informal negotiations failed,” and weaker parties were coerced into accepting a decision favorable the powerful and not complaining about it (Stephens 2003, p. 228). It is important to note, however, that formal legal institutions are typically dependent on even stronger governmental and social powers, especially outside of national and provincial capitals, despite whatever autonomy or independence exists on paper. In many settings, formal legal institutions may be no more, or even less, likely to further the interests of marginalized individuals than their informal counterparts.

The incentives of local-level dispute resolvers might also limit the extent to which their activities reduce economic inequalities. As noted above, because the social authority of the dispute resolver rests on the stability of the local social order (Characteristic 2), rather than on his ability to resolve disputes per se, dispute resolvers in local-level legal institutions generally aim to preserve order, even if this comes at the expense of fairness. In _Forging the Middle Ground_ , there were instances where the local authority seemingly accepted a resolution based on violence or its threat, as in the following case from Panangguan, East Java: This land dispute between Halim (hamlet head) and Amir (Halim’s cousin) occurred in 2001 in Panangguan village, Pamekasan District, East Java. The dispute began when Amir returned to Panangguan after some time away. Upon 16
a cross-sectional regression of onto a constant and 47 country dummy variables and 3 size dummy variables: _._ In the regression, is a dummy variable equal to one, if bank belongs to size group , and zero otherwise. is a dummy variable equal to one, if bank is headquartered in country , and zero otherwise. We impose restrictions in order to avoid multi-collinearity when estimating the parameters of the model. In particular, we impose the country and size effects weighted by the number of banks to be zero _:_ and with and equal to the number of banks in each size category _j_ and country _k_ , respectively. For each period _t_ , we run a cross-sectional regression to estimate the coefficients, , and . For each individual bank belonging to country _k_ and in size group _j_ , the proportion of systematic variance explained by country effects is approximately given by: The proportion of systematic variance explained by size and global effects are computed in a similar fashion.

|**Country**|**Number of Banks**|**Global Effect**|**Country Effect**|**Size Effect**|
|---|---|---|---|---|
|_Panel A: Regions_|||||
|Africa|34|28.30%|65.00%|6.71%|
|Central Asia & Eastern Europe|62|21.44%|68.23%|10.33%|
|East Asia and Pacific|201|11.84%|83.32%|4.85%|
|Japan|161|11.35%|81.20%|7.45%|
|Latin America & Caribbean|74|18.09%|75.12%|6.79%|
|Middle East & North Africa|65|14.71%|80.51%|4.78%|
|North America|964|44.19%|43.30%|12.52%|
|South Asia|47|15.19%|80.32%|4.50%|
|Western Europe|300|13.98%|77.93%|8.09%|
|_Panel B: Asset Size ($ billions)_|||||
|Assets less than $10|1464|54.76%|36.70%|8.54%|
|Assets larger than $10 but less than $50|495|23.78%|61.28%|14.94%|
|Assets larger than $50|276|17.22%|56.85%|25.93%|

# **Table 6: Time-series Analysis**

This table shows the regression estimates from equation (8) in the paper. Following Bakeart and Wang (2009) we use trend tests to detect potential changes in co-dependence. First, the variance ratio ) is computed for each region each week over 52 week rolling intervals. We use log changes in default probability and include banks with at least 26 observations to 30
Financial Regulation and Government Revenue analogue to our reference because it catches all costs, including rents, local wages, utility bills, equipment, and so on. As well as interviewing banks, we tested the plausibility of this number by using the annual report data and inferred branch costs. In Appendix C, we present a detailed exercise, which backs out the average cost of a branch from the yearly operational expenses of the CBE between 2006 and 2012. In line with interviews with private sector banks, we obtain an average cost of a branch of 303,000 birr. Given that the minimum business-lifecycle of a branch is five years to collect the peak deposit from a location, this makes the average total cost of branch 18 million birr (ranging between 6 and 30), and equivalent to 900,000 USD. Therefore the total cost of opening 91 new branches is 1,638 million birr (ranging between 546 and 2,730).

Similarly to the previous case, we can calculate the revenue gains on the Ethiopian Treasury, by subtracting the NBE bill interest payment from this liability expansion measure. This overall cost is composed of two components: a fixed cost, the installation of 91 new branches, _BI_ ; and a variable cost, which is the net loss incurred by the CBE on collecting 13.976,75 million birr of deposits remunerated at an average rate of 5.4% and their use for NBE bill purchase, which only give a 3% fixed return. Therefore, the final gain can be written as follows which places the revenue gains of introducing the NBE bills at 1,554.2 million birr (between 462.2 and 2,646.2). Overall, this gain is 24% higher than the previous gain and makes the savings of this measure 19% of the deficit and 2.6% of tax revenue.

# **5 Concluding Remarks**

In this paper, we show that the government revenue gains of a specific piece of financial regulation in Ethiopia (the 27% NBE bill regulation) are moderate and that lower bank profits are the channel through which this revenue is created. In order to benchmark the government savings of imposing safe asset purchase on banks, we rely on three credible counterfactuals: 1) issuing a bond competitively priced on international capital markets; 2) raising revenue by diverting resources from the stateowned bank; 3) forcing the state-owned bank to raise new deposits and fund the same bond. Our 18
# **1. Introduction**

While universal social programs—whereby everyone is covered—are excellent at reaching the poorest, the beneficiaries can include many people who do not need this form of public help. Governments have tried many ways of assuring better “targeting,” with the explicit aim of concentrating the benefits of a social policy on poor people. The means used vary in their data requirements, methodological sophistication and costs (both administrative and broader social costs).

Readily measurable proxies for consumption or income are often used in efforts to reduce poverty in settings in which the means-testing of benefits is not an administratively feasible option, as in most low-income countries (and many middle-income countries). Efficiency considerations point to the need for indicators that are not easily manipulated by actual or potential beneficiaries. Proxy variables, such as gender and education, family size and housing conditions, have been common.<sup>2</sup> A score based on these variables is used in validating other targeting methods, such as those based on community-level subjective assessments of who is “poor.” The scores are also entering many social-protection registries—national data bases that are used in various ways including to flag ineligible households in future schemes.

The main challenge has been in setting the score’s weights. Various “poverty scorecards” or “basic needs indicators” have been used. Some versions use _ad hoc_ weights, such as taking a simple average of the scores across components.<sup>3</sup> Practitioners have turned to more sophisticated statistical methods in an effort to further improve targeting accuracy. These methods have come to be known as _proxy means testing_ (PMT).<sup>4</sup> This paper assesses an increasingly popular solution in which the weights in the PMT are identified from regression coefficients for household consumption or income as a function of readily observed covariates. The regression is calibrated to survey data and then used to make the out-of-sample predictions for the relevant population. This has the intuitive attraction that the dependent variable is a

> 2 This idea appears to have emerged in social policy making in Chile in the 1980s (Grosh, 1994, Ch.5). Grosh et al. (2008) provides a useful overview of PMT and other targeting methods found in practice in developing countries, with details on many examples.

> 3 A popular example of the poverty scorecard was proposed by Schreiner (2010); the <u>Progress out of Poverty Index uses</u> Schreiner’s (2015) method. The scorecard includes 10 easily measured correlates of poverty which are used to form a composite index. Diamond et al. (2016) argue that the predictive ability of such scorecards can be improved by calibrating the variables and their weights to local (sub-national) conditions, for which purpose they advocate econometric methods. 4 This term appears to be due to Grosh and Baker (1995, p. ix), who define PMT as “a situation where information on household or individual characteristics correlated with welfare levels is used in a formal algorithm to proxy household income, welfare or need.”

2
Saharan Africa compared to the existing literature, our paper provides the most comprehensive, to date, study of welfare dynamics for the region as a whole.<sup>2</sup> In addition to generating newer and more data, this synthetic panels approach also enables us to offer a more consistent measurement of poverty dynamics since it applies the same methodology and employs the same standard and welfare measure for all countries, which is not the case in most existing studies that use panel surveys. Furthermore, since synthetic panel data are constructed from cross sectional surveys, these data are also exempt from issues that usually plague panel data quality such as attrition.

Our findings suggest that on average—that is when all the 21 countries are taken together— the region experienced pro-poor growth. Even though chronic poverty remains high, one-third of those considered poor in the first period moved out of poverty in the second period, which exceeds the proportion of the population that fell into poverty in the same period. The region also saw a 9 percent (or a five percentage points) reduction in poverty and a 28 percent increase in the size of the middle class, albeit from a somewhat low base. However, the vulnerable category also grew by 12 percent. Our pro-poor growth definition suggests that countries with positive growth are Mauritania, Ethiopia, Togo, Swaziland, Malawi, Chad, Botswana, Ghana, Uganda, Congo DRC, Mozambique, Rwanda, Tanzania, and Sierra Leone. On the other hand, countries with growth that is not pro-poor are Burkina Faso, Zambia, Madagascar, Cote d’Ivoire, Cameroon, Senegal, and Nigeria. There is also some indicative evidence that most resource-rich and middle-income countries have more upward mobility than downward mobility. Post-secondary education is

> 2 Similar analyses using synthetic panel data have been done for other regions such as Latin America (e.g., Ferreira et al., 2013; Vakis et al., 2016) or Middle East and North Africa (Dang and Ianchovichina, 2016). For an analysis of poverty based on asset indexes for 11 countries in Africa in the 1990s, see Sahn and Stifel (2000); but also see, e.g., Harttgen et al. (2013) who argue that asset indexes may not be able to capture the trends in welfare over time as consumption-based measures do.

3
heterogeneous, so that a larger number of additional voters may be attracted from a reduction in the gasoline price, even when this price is initially quite low.<sup>24</sup> Thus overall, one cannot say too much about the (directional) relationship between car ownership and motor fuel subsidies from theoretical arguments alone. It could be that, when comparing democracies and more autocratic governments, subsidies to motor fuels are likely to be relatively more prevalent in the former relative to the latter, when broader groups own motor vehicles; while the opposite could be the case when the group possessing motor vehicles is small. The reason is that with a broad group of vehicle owners, a large number of voters are affected by a given fuel subsidy rate. This may be the dominating factor in many democracies where leaders may need a large core group to stay in power. In autocracies, by contrast, the power base of leaders is often narrower: this makes fuel subsidies attractive for autocracies when few (basically, all in the core support group) own cars. Moreover, the fiscal cost of paying these off through low fuel prices will then be relatively low.

Thus while these relative effects are difficult to sort out in a theoretical model, they can be tested, which I intend to do on our compiled data set. In particular, one can test a) if the propensity to subsidize motor fuels is greater or smaller when the group of vehicle owners is larger; and b) whether this relationship differs between democracies and autocracies, and according to the “strength” of democracy as defined in our data.

Note finally the argument, made by some observers, that political competition models as presented here yield meaningful explanations of political outcomes only when the group of voters at stake (here, the group of car owners) is relatively large. But note that there are here both political benefits (more favorable voters) and costs (fiscal expenditures) associated with fuel subsidies when this group is large; and not obvious in which direction a larger car-owning group should pull. List and Sturm (2006) show that narrowness of this group does not preclude variables directed specifically at this group from having a significant political impact. This we also assume here and in the following.

# **3. Effects Based on Middle Class Preferences When Influence Activities Are Included**

In this section we extend the analysis to take into account possible influence activities by the middle class. This involves bribes, _B_ , now being endogenous and set to optimally influence the policies of government.<sup>25</sup> This is manifested in (1), by assuming that _B_ is now set by middle class households as a function of the levels of _qG_ and _XM_ delivered. We assume that only those

> 24 In any case, voting is likely to be quite heterogeneous and in most cases far from fully aligned with what are presumed basic interests; see e.g. Huber and Stanig (2009).

> 25 The model framework in this section becomes, in many ways, similar to the set of models of “influence activities” in chapter 7 of Persson and Tabellini (2000).

13
in treated markets and it captures both the impact on existing facilities as well as changes in facility composition due to exit or entry.<sup>20</sup> _Xh_ are facility or market-level covariates, and _εh_ are unobserved characteristics. Since we stratified by county-market size groups, we follow Bruhn & McKenzie (2008) and include _Vhj_ , which is a dummy variable equal to one if the facility is in one of the randomization strata _j_ , where _n_ = 16. Standard errors are clustered at the market level, unless otherwise stated. To account for multiple hypothesis testing, we also report sharpened twostage q-values for the main outcomes of interest in braces, following Benjamini et al. (2006) and as described in Anderson (2008). Finally, we present both unweighted and weighted estimates at the facility level, where the weights are the patient load. The former relates to standard models in the IO literature, where quality and price are facility characteristics and demand is endogenous, while the latter show the impact on the average patient and is therefore what is important for the patient’s welfare.

We further estimate the heterogeneity of impacts, using the following specification: Here, _Whk_ is a binary variable, indicating whether the observation belongs to one of the subgroups over which we are running the heterogeneity analysis, for instance, whether a facility is private or unlicensed. All other notations are similar to Equation 1. We first report the impact of the treatment on facilities with _endline_ characteristic _k_ in treated markets. This is the relevant policy parameter of interest, and answers questions of the type: “What is the difference in the quality of unlicensed facilities in treatment versus control markets?” It is not the causal impact of the treatment on facilities with characteristic _k_ , which at endline is endogenous to the treatment itself.

We therefore also report the causal impact of the treatment on facilities with characteristic _k_ at baseline. In this case, the treatment effect is most precisely reported for the likelihood of exit and patient load; for the latter, we can correctly assign a value of zero when the facility is closed. For other characteristics, such as the JHIC score, we will have missing data for the 16% of all facilities in the census at randomization that exited by endline, and although we present these results in the appendix, they come with the caveat that they pertain only to surviving facilities. With this high rate of exit, any estimates based on bounds will be quite imprecise, underscoring the importance of the market-level randomization, which still allows us to back out the policy relevant impact of the treatment on regulated markets.

> 20The treatment estimators thus correspond to population intent-to-treat, but due to the high take-up and adherence to treatment status, as well as the high response rate at endline (97% of the census of facilities), they are unlikely to differ from treatment-on-the-treated effects.

17
The advantage of the LiTS data is that it provides us with comparable data on the impact of the recent crises for a representative sample of households in a large number of countries. That said, the cross-sectional nature of the data limits the extent to which the correlations observed in the data may be interpreted as causal relationships. At the household-level, we cannot rule out that the exposure of households to income shocks and their reaction to these shocks may both be driven by unobserved household characteristics. At the country-level, we cannot rule out that the observed relations between the monetary regime or banking sector structure and household reaction to income shocks may be driven by a wide range of other differences in the macroeconomic and institutional environment across countries. For these reasons the results presented below should be interpreted with caution.

# **3.2 Which Households Were Hit the Most?**

The studies surveyed in section 2.4 suggest that the impact of financial crises on household income, consumption, health and education may vary according to the income level and location (urban versus rural) of households. In this section we examine whether these patterns are confirmed by the LiTS data for the recent banking crises in the ECA region. We hereby focus our analysis on the impact variables _Income shock_ , _Staple foods_ , _Other consumption_ and _Health_ , comparing these for households by rural / urban location and income level prior to the crisis.<sup>12</sup> We provide separate analyses for high-income crisis countries, middle-income crisis countries and non-crisis countries.

The sub-sample means presented in Table 4 suggest that in the **high-income crisis countries** rural households were hit harder by income shocks (46%) than urban households (33%). As a consequence 15% of rural households cut back on staple food consumption and 62% cut back on non-essential consumption goods compared to only 9% and 47% respectively among urban households. In the high-income crisis countries, households of all income-levels are equally likely to be hit by an income shock. Not surprisingly though, income shocks have different consequences households according to their income level: Households in the lowest income-quintile are much more likely to reduce staplefood consumption than households in higher income quintiles.

Table 4 shows a completely different impact on households in **middle-income crisis countries** compared to high-income crisis countries. In line with the evidence for other emerging markets (see section 2.4) we find that in the middle-income countries urban and high-income households were more likely to experience income shocks and were more likely to cut back on non-essential

> 12 Each household head was asked where their household was positioned on the national income ladder (on a scale of 1-10) in 2006 relative to other households in their country. We use this subjective measure of income as opposed to current expenditures as it gives us an assessment of the income position prior to the crisis.