rafmacalaba/datause-encoder-data huggingface dataset:
mixed results regarding the effect of the minimum wage on the employment of young workers. In Poland, the period 2005‐2010 saw a relatively rapid rise in the minimum wage in parallel with a significant decline in the employment of 15 to 24 year‐olds. The increase was so high that the ratio between the minimum wage and the average wage went from 0.34 to 0.41 in less than five years. Since the increase was uniform throughout the country, it was estimated that people in the poorest regions were most adversely affected (Majchrowska and Zołkiewski (2012). The negative impact on young workers was strongest in the less advanced regions and where the ratio between the minimum wage and the average wage was relatively high (Broniatowska et al., 2015).

For the United States between 1954 and 1979, Brown et al. (1982) noted that a 10 percent increase in the minimum wage generated a 1 to 3 percent reduction in the employment of young workers. Similarly, a more recent study by Neumark (2014) observed an overall reduction in employment following an increase in the minimum wage and young workers were affected the most. Studies on Brazil by Fajnzylber (2001) and Lemos (2004) also found greater job losses among young workers than for the workforce in general.

The evidence from some countries indicates that when faced with minimum wage increases, businesses tend to replace marginally productive low‐skilled workers whose performance is below minimum wage level with more skilled workers. In Portugal, for example, Pereira (2003) analyzed the impact of a minimum wage equalization policy for young workers compared with the minimum wage level for workers over 19 years old. Based on panel data from a number of businesses, this study found that 10 percent increases in the minimum wage reduced employment for workers 18 and 19 years old by 2 and 4 percent, respectively, whereas they actually increased employment for workers 20 to 25 years old. This study also found a significant reduction in hours worked or cutbacks from full to half‐time work. Faced with an imminent increase in labor costs, businesses replaced less skilled workers (18 and 19 year‐olds) with workers who were more skilled (20 to 25 year‐olds). In Chile, Montenegro and Pagés (2004) found that the minimum wage had a negative effect on the employment of young low‐skilled workers over the period 1960‐1998.

Recent studies on Costa Rica and Honduras by Gindling and Terrell (2005, 2009) found that the minimum wage had similar adverse effects for less skilled workers. Based on information from household surveys over the period 1988‐2000, Gindling and Terrell (2005) found that a 10 percent increase in the minimum wage generated a 1.09 percent contraction in employment and 0.6 percent reduction in the number of hours worked. The study also examined the effects at different points in the range of skills, finding that the minimum wage disproportionally affected workers in the middle and lower range (from the second to the fifth decile). Overall, the evidence for Costa Rica suggests that businesses adapt to increases in the minimum wage by replacing less skilled workers with those who are more skilled.

14
surveys relating to governance are very costly to design and implement, and as a result typically cover a much smaller set of countries than polls of experts.

Sources of governance data also vary with respect to the sample of countries they cover. A number of sources cover a very large sample of developed and developing countries (EIU, DRI, HFWSJ, PRS and WDR), while others cover very narrowly-focused samples of countries (PERC for Asia, CEER and FHNT for transition economies). Some sources cover primarily developed countries but also include major developing countries (WCR, GALLUP, BERI). Since there is a strong positive association across countries between governance and per capita incomes, this difference between sources makes it difficult to compare indicators from sources which cover sets of countries with very different income levels. Similarly, there may be regional differences in govemance which hamper comparisons across sources. For example, it is not clear how to compare a governance rating based only on transition economies with one based on a broad set of countries. As discussed in our companion paper (Kaufmann, Kraay and ZoidoLobat6n (1999)), the methodology we use to construct aggregate govemance indicators takes these differences in country coverage into account. Users of the govemance database are also encouraged to keep this consideration in mind when comparing information from different sources.

In order to distinguish between indicators according to the representativeness of their country coverage, we construct a simple index which measures differences between the distribution of countries across income and regional classifications and the corresponding distribution of all countries in the world. In particular, we divide the world into a two-way classification by region and income, following the World Bank's 1998 World Development Report. For each of the sources of govemance data, we report onehalf of the sum of absolute values of the deviations between the share of countries in each of the 45 categories (five income categories x nine regions) in that source and in the world as a whole. By construction, this measure ranges from zero to one, with low values indicating more representative indicators. We report this number in the fifth column of Table 1. The six indicators covering the largest number of countries (DRI, EIU, FH, HFWSJ, PRS and WDR) are substantially more representative according to this measure than the others, with a value of this index of less than 0.25. We refer to these as representative indicators, and the remainder as non-representative indicators.

6
# **Table 8 Why Don’t People Have Bank Accounts?**

||**Percentage**<br>**among the un-**<br>**banked**|
|---|---|
|**What are the main reasons why you do not have a bank account?**||
|Do not have the amount of moneybanks require to open an account|25.0%|
|Bank fees are too high|16.5|
|Are notquite sure how to open an account|6.7|
|Banks hold checks for too long|2.3|
|Banks are not located conveniently|2.6|
|Banks are not open whenyou need to use them|2.1|
|Most bank staff onlyspeak English|1.5|
|None of the reasons listed above|57.9|
|**Which bank fees are too high?(among those citing bank fees as a barrier)**||
|Monthlyaccount fee|55.4%|
|Bounced check fee|29.8|
|Per check fee|21.8|
|Fee for use of "foreign" ATMs|16.9|
|Annual fee for ATM card|4.7|
|Other fee|24.2|
|Have heard of "basic" checking accounts that charge low fees, set low minimum<br>balancerequirements, and permit you to write alimitednumberof free checks|76.6|
|Have never had a bank account|63.3|

Because of the shortcomings of the OCC survey regarding the reasons that people do not have a bank account, we include the results from one other survey that addressed the same issue. In a 1996 survey of 900 lower-income urban households, Caskey (1997) asked households without deposit accounts, why they do not have an account. He provided respondents with a list of possible reasons from which they could select one or more. They could also provide a reason that was not on the list. As shown in Table 6, 53 percent of the respondents cited "don't need account because we have no savings" as a reason, making this the most frequent reason cited; another 45 percent cited bank fees or minimum balance requirements.

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school feeding in primary and junior secondary schools, and one study on distance education in primary schools. Each of these studies provides estimates of the impact on test scores from a well-defined intervention, but none follow their study participants long enough to estimate the impact on future labor earnings. To go from test scores to monetary benefits, we rely on the nonexperimental work of Evans and Yuan (2019), who estimate the effect of improved test scores on future labor earnings in Ghana and elsewhere.

With respect to the quantity of schooling, we found only one experimental study, Duflo, Dupas, and Kremer (2021), that assesses the impact of additional years of (senior secondary) schooling. This study does follow study participants for many years, but it remains incomplete in the sense that some of the study participants have yet to begin working. Perhaps because of this, the study finds no impact from increased secondary schooling on labor earnings, a result that runs counter to our prior beliefs about the value of schooling.

To complement that study, then, we take a more traditional, nonexperimental approach to estimating the benefits of an additional year of public schooling, so-called Mincer regressions (Patrinos and Psacharopoulos 2018). The limits of this approach are long debated (e.g., Card 1999) and we review them here. But we view it as our best option.

All the results we use, including the experimental ones, are vexed by the problem that there is a long lag between going to school and the labor earnings that one eventually gains from that schooling. For cross-sectional estimates such as our Mincer equations, this means that we are estimating the gains that today’s students will achieve in the future based on today’s labor earnings of those who went to school many years ago. But even for experimental studies such as Duflo, Dupas, and Kremer, any eventual estimates of the impact of additional years of schooling on future labor earnings will be for students who went to school circa 2012. These may not be externally valid for students in school at the time when the researchers eventually gather data on labor earnings for the past students in the study sample.

Overall, we find that public spending toward the quantity and quality<sup>5</sup> of schooling offers good value for money: All our benefit-cost ratios exceed one. But we also find that all our benefit-cost ratios are modest when compared to some of the more spectacular ratios found in a typical Copenhagen Consensus study like the Ghana Priorities project. However, most of the

> 5 This being limited to quality improvements we can study carefully: remedial education and school feeding.

3
TABLE VI: Heterogeneous Income and Price Effects

||(1)|
|---|---|
|tc|0.0174***<br>(0.006)|
|tu|0.0182*<br>(0.011)|
|tc_×_ y<sup>_f_</sup>|-0.000272*<br>(0.000)|
|tu_×_ y<sup>_f_</sup>|-0.000281<br>(0.000)|
|tc<sup>2</sup>|0.0000488<br>(0.000)|
|tu<sup>2</sup>|-0.00118<br>(0.001)|
|tc_×_ tu|0.00000588<br>(0.001)|
|y<sup>_f_</sup>|0.00399<br>(0.004)|
|Observations|17432|
|R-squared|0.124|

_Note:_ Standard errors are clustered at the locality level and are presented in parentheses. * _p <_ 0 _._ 10, ** *** _p <_ 0 _._ 05, _p <_ 0 _._ 01. Dependent variable: _Enrollit_ . Sample: unbalanced panel of children aged 12-15 years in 1997-1999 from eligible (poor) households with two parents and one parent reports to be the head of the household. y<sup>_f_</sup> denotes father’s weekly per-capita income; tc (tu) denotes the weekly, offered per-capita CCT (UCT). We instrument for father’s per-capita income with average locality wage (excluding the wage of the father in question), and we instrument for _tc × y_<sup>_f_</sup> and _tu × y_<sup>_f_</sup> with the offered CCT and UCT interacted with the average locality wage (excluding the wage of the father in question). Regressors not shown: child age dummies, highest grade completed dummies, age interacted with highest grade completed, year dummies, and a child fixed effect.

We proceed to calculate moments of the income and price effect schedules (see Appendix B.2 for explicit calculation of moments). Moments are presented in Table VII below. We find a significant average price effect of 0.010, and an average income effect of 0.0037. We then estimate the average value of the ratio of the income effect to the price effect using the second-order Taylor series expansion given by Equation (13) below.<sup>31</sup> We find the average of this ratio is equal to 0.21. Finally, in Appendix B.4 we allow for additional heterogeneity in price and income effects with respect to child age and child gender. We do not find statistical evidence to support heterogeneity in these additional factors. Our moment estimates are robust to this more flexible specification.

31. E <u>�</u> _PI_ �� (( _XX_ <u>)) �</u> will be a biased estimate of E � _PI_ (( _XX_ <u>))</u> �. Instead we evaluate the second-order Taylor _I_ <u>(</u> _X_ <u>)</u> series expansion of E � _P_ ( _X_ ) �. We adjust second-order moments of income and price effects used in this expansion for bias (see Appendix B.2 for calculation of second-order moments).

33
**Table 7: Comparing Weighted Risk Adjusted IGRC to Canonical IGRC**

||**CH**<br>|**INA**<br>|**IND**<br>|**IA**<br>|**INDO**<br>|**NESIA**<br>|
|---|---|---|---|---|---|---|
||Weighted<br>RIGRC|Canonical<br>IGRC|Weighted<br>RIGRC|Canonical<br>IGRC|Weighted<br>RIGRC|Canonical<br>IGRC|
|All|0.484|0.383|0.876|0.621|0.568|0.497|
|Urban|0.420|0.356|0.721|0.563|0.527|0.468|
|Rural|0.436|0.321|0.863|0.589|0.532|0.467|
|Sons|0.402|0.329|0.800|0.595|0.524|0.461|
|Daughters|0.571|0.438|0.980|0.643|0.607|0.528|
|Urban Sons|0.351|0.312|0.651|0.524|0.498|0.443|
|Urban Daughters|0.486|0.402|0.791|0.597|0.551|0.489|
|Rural Sons|0.357|0.270|0.829|0.592|0.487|0.431|
|Rural Daughters|0.519|0.375|0.921|0.580|0.571|0.500|

_Notes_ : (1) The data are from children who were born between 1950 and 1989 using the CFPS 2010 round for China, the IHDS 2012 round for India, and the IFLS 2014 round for Indonesia. (2) The weights are the proportion of children at each level of father’s education.

**Table 8: Evolution of Risk Adjusted IGRC by Birth Cohorts**

||**CH**|**INA**|**IND**|**IA**|**INDO**|**NESIA**|
|---|---|---|---|---|---|---|
||Weighted<br>RIGRC|Canonical<br>IGRC|Weighted<br>RIGRC|Canonical<br>IGRC|Weighted<br>RIGRC|Canonical<br>IGRC|
|1980-1989|0.507|0.420|0.705|0.551|0.468|0.424|
|1970-1979|0.493|0.398|0.822|0.582|0.540|0.492|
|1960-1969|0.369|0.292|0.993|0.650|0.704|0.586|
|1950-1959|0.399|0.292|1.054|0.681|0.597|0.521|

_Notes_ : (1) The data are from children who were born between 1950 and 1989 using the CFPS 2010 round for China, the IHDS 2012 round for India, and the IFLS 2014 round for Indonesia. (2) Each row uses a subsample of children who were born in the given birth cohort. (3) (2) The weights are the proportion of children at each level of father’s education.

32
# **3.4 Post-experiment**

The interpretation of our estimates depends on what benefits children received between the experiment and the observed ENLACE tests. Self-reports from the follow-up survey show that households in treatment villages (both in-kind and cash) reported receiving on average 12 months of PAL aid, however we do not have household level information on the type of transfers received after the follow-up survey.

SEDESOL was able to provide us only with village-level administrative counts of the number of beneficiary households per year receiving PAL, _Oportunidades,_ or _Liconsa_ between 2005 to 2013. Figure 1 plots the average number of beneficiaries of PAL, _Oportunidades,_ and _Liconsa_ over time for the three experimental groups. While the average number of PAL beneficiaries fluctuated between 200 and 50 for in-kind villages and between 250 and 50 for cash villages, the control villages remained with an average number of beneficiaries below 50 during the entire period (left panel in Figure 1). The number of beneficiaries of _Oportunidades_ and _Liconsa_ steadily increased over time. Cash localities displayed on average a lower number of households that are beneficiary of the _Oportunidades_ transfer (middle panel in Figure 1). This difference, that is very small in size,<sup>15</sup> is likely to partly reflect differences in population. In fact, both in 2005 and 2010 - years for which the population census is available - we find that the number of households in in-kind and cash localities is lower than in control ones (see columns 1 and 4 in Appendix Table A1), possibly as a result of differential migration. The share of beneficiary households in neither of the treatment groups is statistically different from the one in the control group (columns 3 and 6 in Appendix Table A1).

Overall, the evidence presented in this section suggests that our estimates should be interpreted as the combined effect of differential exposure and differential take-up in treatment and control localities.

If the receipt of other programs after the experiment is correlated with the treatment assignment to the villages and those programs affect student performance outcomes, then our results would reflect not just the impact of initial transfer modality, but also the dynamic response to that initial treatment.

> 15On average cash and in-kind localities have 12 and 4 recipients fewer than the control group, that on average has 62 households that are _Oportunidades_ beneficiaries. Since the follow-up survey, on which the merge is based on, samples 33 households (about 20 percent of the total number of households), differences in the number of _Oportunidades_ beneficiaries are likely to lead to very small differences in terms of children who have to comply with the attendance conditionality in our sample.

12
labor productivity variables, these product flows are aggregated into five-year periods from 1980–1984 to 1995–1999 and then first differenced in log format. Each productivity growth observation available with the UNIDO dataset is paired with industry-level bilateral export observations from that country. All exporting countries other than the United States are included.

The majority of export volumes for bilateral routes are zero-valued, which creates challenges for the estimation of equation (3). It is also the case that the minimum threshold of trade that can be consistently measured across countries and industries is US $100,000 in the WTF database. While Feenstra et al. (2005) are able to incorporate smaller trading levels for some countries, these values are ignored to maintain a consistent threshold across observations. To accommodate these conditions, the empirical approach separately studies the extensive and intensive margins of export expansion. Mean export volumes are taken across exporter-importer-industry observations for fiveyear time periods. For the extensive margin, entry into exports along an exporterimporter-industry route is defined as exports greater than US $100,000.

# _US Historical Settlement Patterns_

The first building block for the instrument is the historical settlement patterns of migrants from each country _M_ % _i_ , _c_ ,1980 . These data are taken from the 1980 Census of Populations, which is the earliest US census to collect the detailed ancestry of respondents (as distinguished from immigration status or place of birth). The detailed ancestry codes include 392 categories with positive responses, and this study maps these categories to the UNIDO records. Respondents are asked primary and secondary ancestries, but the classifications only focus on the primary field given the many missing values in the secondary field. There are multiple ancestry groups that map to the same country, but the mapping procedure limits each ancestry group to map to just one UNIDO country. Categories not linked to a specific UNIDO country are dropped (e.g., Western Europe not elsewhere classified, Ossetian). In total, 89% of the US population in 1980 is mapped.

Metropolitan statistical areas, which will be referred to as cities for expositional ease, are identified using the 1% Metro Sample. This dataset is a 1-in-100 random sample of the US population in 1980 and is designed to provide accurate portraits of cities. The set
overlap component (43.3 and 47.2 respectively over the same periods). This highlights the existing regional disparities inside Jordan that are largely explained by differences in the level of consumption between these regions rather than a redistribution of welfare within them. Nevertheless, the decline of the between-group inequality over time points to a decline in those regional disparities and therefore a convergence among governorates in terms of consumption levels. This again reflects some success of the strong economic performance over the past decade in providing a more equitable welfare growth among the various governorates of the Kingdom.

|**Table 6: Deco**|**2002**<br>**mposition of t**|**2010**<br>**he Gini Coeffi**|**2002**<br>**cient by Popu**|**2010**<br>**lation**|
|---|---|---|---|---|
||**_Le_**|**_vel_**|**_Contribu_**|**_tion(%)_**|
|**Kingdom**|0.345|0.329|100|100|
|**Urban-Rural**|||||
|Within|0.235|0.245|68.2|74.4|
|Between|0.043|0.030|12.6|9.2|
|Overlapp|0.066|0.054|19.2|16.4|
|**Governorates**|||||
|Within|0.082|0.082|23.7|25|
|Between|0.114|0.091|33.0|27.8|
|Overlapp<br>Source: World Bank Staff|0.149<br>Calculations using O|0.155<br>fficial Household I|43.3<br>ncome and Expend|47.2<br>iture Surveys.|

As addressed next in the paper, these findings are partly attributed to policy decisions taken in the country to redistribute the economic returns of this boom towards governorates using mechanisms such as cash transfers, education and health services and more importantly public sector employment. While these tools have had some success so far, they come at a very high fiscal cost and have reached their limits. The economic crisis in the country since 2009 has revealed the weakness of these tools in addressing equity concerns, and their fiscal costs have indeed exacerbated macro volatility in the country, therefore jeopardizing recovery in economic activity and long-term sustainable future growth<sup>41</sup> . It can be argued that since these tools have not been utilized extensively since 2009, as it did previously in the decade, it has contributed to reversing the pro-poor economic growth trend<sup>42</sup> . This has therefore contributed significantly to the general population’s perception of increased inequality and poverty. Having said this, the

> 41 Refer to the World Bank’s Jordan Development Policy Review (2012) for an extensive analysis of the role of macro volatility, fiscal policy, public sector employment, subsidies, trade, service delivery, and political reforms on Jordan’s economic growth and competitiveness.

> 42 As explained in previous sections.

21