rafmacalaba/data-use-mentions-extended huggingface dataset:
related to the economy? Returns are higher for direct investments that are held for a longer period of time, as well as for smaller investments. We are also able to investigate differences in returns across sectors, including those considered especially conducive to economic development, such as financial institutions (Levine 2005) and infrastructure (Aschauer 1989, Roller and Waverman 2001). Ultimately, while sector explains much less variation in performance than geography, we find that investments in financial institutions, infrastructure, and mining have higher returns than agribusiness and services.

Beyond private equity specifically, our work contributes to a smaller, more recent literature examining the return and risk of impact investing strategies. The IFC, created to advance economic development, was one of the first investors to measure social outcomes associated with its investments. Its charter, which requires that investments be made with the intent to promote economic development alongside financial profit, aligns closely with the standard industry definition of impact investing.<sup>4</sup> There is little evidence regarding the financial and social performance of impact investment strategies. Brest et al. (2018) argue that impact investors, because their deployment of capital in pursuit of social or environmental goals leads them to invest in projects that would not have been financed otherwise, earn lower risk-adjusted returns than traditional investors. Barber et al. (2020), comparing data for a similar set of non-impact funds to data obtained from PreQin on 159 impact funds between 1995 and 2014, find the latter to achieve, on average, a 4.7 percentage point lower IRR. Jeffers et al. (2024), independently assessing the performance of venture capital impact investment funds that target market returns, find that although such funds underperform the market, they also incur less risk than traditional venture capital funds. Cole et al. (2023) study whether impact investors deploy capital in different industries and locations compared to traditional investors, finding impact investors are more likely to invest in poorer areas and nascent industries. Our paper provides
Our data come from trade records of the United States, classified at the 10-digit level of the Harmonized System (HS) of trade classification. We use monthly frequency import data from January 2002 to April 2011. The data was obtained from the Foreign Trade Division of the U.S. Census Bureau. From these data, prices were computed as the ratio of import values to quantities. These unit values are used as our proxy for goods prices.

In total, the dataset covers 26,459 product categories. However, not all categories have price information; 7,976 products do not. Also, the analysis of volatility requires data for extended periods of time, and we dropped products that do not have price data for at least 36 consecutive months. The final data set thus covers 12,955 products.<sup>3</sup> Our benchmark analysis focuses on U.S. imports data rather than on exports data for two reasons. First, the reporting of imports data is generally less subject to measurement errors than exports data, as imports are more subject to tariffs and inspections than exports. Second, U.S. imported products are more numerous and diverse than exports. In fact, the U.S. reports twice as many imported as exported goods. Also, 17 percent of imports are commodities compared to only 4 percent for exports. While studying the pattern of US exports may be relevant for a U.S. specific analysis, it is essential for our general analysis to use imports data.<sup>4</sup> It is noteworthy that this sample period covers years of historically high volatility of real commodity prices, perhaps only surpassed by the early 1970s (see, e.g., Calvo-Gonzalez et al. 2010). Consequently, if there is a period selection bias in the data, it would probably bias

> 3 The results reported below are unaffected by alternative choices of datasets such as keeping products with price data available throughout the whole sample
5.2|5.3|
|F-frst stage IT*competition|10.3|12.5|13.4|14.0|13.6|13.3|
|Sargan|0.62|0.60|0.84|0.93|0.93|0.91|
|Controls|||||||
|Age|No|Yes|Yes|Yes|Yes|Yes|
|Firm size|No|No|Yes|Yes|Yes|Yes|
|Share of white-collar workers|No|No|No|Yes|Yes|Yes|
|Capital/worker|No|No|No|Yes|Yes|Yes|
|Exports/sales|No|No|No|No|Yes|Yes|
|FDI share|No|No|No|No|Yes|Yes|
|Time efects|No|No|No|No|No|Yes|
|Observations|1402|1402|1402|1402|1402|1402|

Robust standard errors in parentheses * _p <_ 0 _._ 10, ** _p <_ 0 _._ 05, *** _p <_ 0 _._ 01 All specifications include firm’s fixed effects. Source: Authors’ calculations using data from ENTIC, INEGI

# **5.4 Robustness tests**

In order to analyze the robustness of these results, all the equations were estimated using pooled regressions instead of fixed effects to test the sensitivity of our results to unobserved heterogeneity. Even though coefficients from the pooled regressions are slightly higher in all cases, the conclusions and statistical significance do not change.<sup>11</sup> With the purpose of analyzing what previous studies, such as Bloom et al. (2012b) have found regarding the relation between management and IT use and how these two factors combined enhance productivity, we included an interaction of IT use and a proxy for
students who were not currently migrants, 16 percent in Micronesia and Papua New Guinea, 20 percent in Tonga, and 32 percent in Ghana said they had changed in part what they studied, or studied extra because of the prospect of potentially migrating. The channel for them though is not so much in terms of attainment, as in what they study – more report studying foreign languages and taking test preparation classes to pass entrance tests abroad. In some of these countries we also did surveys of teachers of 10<sup>th</sup> to 12<sup>th</sup> grade in the top secondary schools to see whether they taught anything differently as a result of the possibility their students may migrate. In Micronesia, 35 percent of teachers say they teach things they wouldn‘t otherwise do: examples include U.S. history and culture, foreign languages, tolerance of different perspectives, and botanical procedures for plants grown abroad. In Papua New Guinea, where 27 percent of surveyed teachers say they teach material they wouldn‘t otherwise, coverage of exchange rates and international trade, and human resources and labor exports are mentioned.

It is notable that most of these responses in terms of new human capital acquisition in our survey data are for knowledge that in large part only has its main payoffs abroad (although there will also be some benefits in the home country for those individuals whose jobs involve considerable contact with the outside world). This critique of brain gain theories is often raised with regard to medical migration, where it is noted that the prospect of migration may induce over-investment in fields like geriatric medicine which have high demand abroad, at the expense of fields like tropical medicine which have the greatest needs at home but little payoff abroad. We are unaware, however, of any research which goes beyond anecdote and description in this regard, so are unsure as to how serious an issue this is in practice. Nonetheless, in addition to the lack of supply elasticity and ease of movement for
and adverse distributional effects (Bromley 2009). Distinguishing policy or regulatory reform from titling and showing that these have very different land market activation effects allows us to reconcile these views. We document robust land market effects that can be unambiguously attributed to regulatory reform which, by reducing transaction costs, increased the number of registered transfers and mortgages for parcels that had already been registered or were registered sporadically in response to this policy change. This makes our paper the first to document robust credit market effects from regulatory and institutional reform. Our finding that (subsidized) systematic titling had a negative net impact on land market activity suggests that land market activation is best achieved via policy reform.

Second, while a large literature suggests that women having formal land rights enhances their well-being by increasing investment (Ali _et al._ 2014), labor force participation (Newman _et al._ 2015) and bargaining power (Menon _et al._ 2014), less is known on what is needed for women to have their land rights documented and participate in markets in the first place. Results suggest that legal change can help increase female land ownership, its full potential will be realized if combined with other measures. While in our case this was performed by systematic registration, financial incentives or nudges to include women on title documents (Ali _et al._ 2016) may be equally or more effective once regulatory reforms have been enacted.

Third, compared to an upsurge in the use of administrative data including for evaluating large programs (Muralidharan _et al._ 2016) or assessing tax compliance (Pomeranz 2015), the advantages of registry data in terms of frequency, granularity, reliability and zero marginal cost to evaluate land programs have not been fully realized with studies mainly remaining at a descriptive level (Ali _et al._ 2017; Holden and Tilahun 2020). We show that econometric analysis of spatially aggregated registry data can help identify impacts of policy reform that elude a traditional DID approach, in addition to remedying some of the shortcomings of
falls by a factor of three. The household level model performs well in this stylized setting because the residuals are distributed normally by construction, and a large percentage of variation in simulated welfare is explained by the two predictor variables. It is reassuring, though, that the small area estimator performs well in a favorable controlled environment with populations that vary across simulations.

# b. Design-based simulation

While model-based simulations are useful to explore the performance of the estimator in different populations, the results of model-based simulations inevitably depend on the set of assumptions used to construct the simulated data. To verify that the household-level model works well when estimated in multiple samples, this section describes the results of a design-based simulation. To reduce computation time, the simulation is limited to three regions in Northeast Tanzania near the Kenyan border: Arusha, Kilimanjaro, and Tanga. Between them, these three regions according to the census contain 24 districts, 2,078 villages, 10,964 enumeration areas, and nearly 1.17 million households.<sup>38</sup> The 2018 Household Budget Survey sampled 1,217 households in 97 enumeration areas from these three regions, for an average sample of 12.5 households per enumeration area. The three regions are disproportionately poor, as the non-monetary poverty rate is 46.5 percent when using a poverty line set at the 20<sup>th</sup> percentile of the national distribution.

To conduct the design-based simulations, we repeat the following seven-step procedure 250 times:

1. Draw a simple random sample of 4 EAs for each of the 24 districts from the census, which selects a total of 96 EAs from the population of 10,964 census EAs contained in the three regions.

2. Draw a simple random sample of 13 households for each selected EA to generate a sample of 1,248 households.

3. Construct sample weights for each household equal to the inverse of their selection probability.<sup>39</sup> 4. Use the ordered quantile
CEE and all-Europe specifications and are even above 50 for the non-CEE sample. This is much larger than the 12-28 range for a weak-IV F-statistics in Kraay (2014) and well above Staiger and Stock’s (1997) rule of thumb of 10.

Country-level multiplier estimates (Columns 4-6) are generally larger than those at the subnational level, though they are typically less than one, more noisily estimated and significant only for the all-Europe sample. We focus on the all-Europe sample first, as with annual country-level data sample size is a limiting factor; wider standard errors lead to a general lack of significance for the country-level split CEE/non-CEE sample. For the OLS specification, the whole-Europe multiplier is 0.8 and is significant at the 5% level (Panel A, Column 4). The all-Europe IV estimates are marginally smaller at 0.67, but 50% wider standard errors mean significance is now at the 10% level. The first-stage coefficient is smaller than for the NUTS2 subnational regressions, but still large ( = 0.8 ), with a first stage F-statistic above 80. As foreshadowed earlier, both CEE and non-CEE multipliers are always insignificant, however the CEE point estimates are larger than those for θθ<sup>�</sup> the non-CEE group. The insignificance of the CEE 2SLS multipliers is because the first stage is weak.<sup>46</sup> _Robustness to reported EU spending._ In the discussion above, we emphasized that one advantage of our approach was using modeled rather than reported EU spending, which is likely to be closer in time to when the actual spending takes place. In Online Appendix Table A3.1 we re-estimate our results using reported EU spending. At the NUTS2 level for All-Europe and non-CEE, results are fairly similar: small or insignificant multipliers at the 5% level for OLS and IV specifications. However, at the NUTS2 level for CEE countries the raw spending multipliers are sometimes a little higher, though never close to 1. More
While such impediments are both explicitly discriminatory and non-discriminatory in character, those targeted specifically at foreign investors raise the cost of entry and limit the competitiveness of foreign invested firms once established. Such ‘trade costs’ are arguably more significant, and potentially more FDI-inhibiting, than the non-discriminatory ‘doing business’ impediments stemming from undue red tape or unduly onerous regulatory requirements that weigh equally on established foreign and domestic firms.

**Figure 16. Restrictiveness of services trade policies by sector and modes of supply, 2018**

<!-- Start of picture text --> 0.25<br>0.2<br>0.15<br>0.1<br>0.05<br>0<br>Mode 1 Mode 3 Mode 4 Overall<br><!-- End of picture text --> Source: OECD services trade restrictive index (STRI) 2018 It bears noting that the scope and focus of the concept for trade facilitation in goods embedded in the TFA has a very different context from the discussion now emerging for trade facilitation in services and investment. While the process of liberalization of trade in goods started with GATT more than half a century ago, the process of promoting the full transparency and liberalization of measures affecting international trade in services is of more recent vintage. Furthermore, 25 years after the negotiation of the General Agreement on Trade in Services (GATS), the level of market-opening progress reached on this front has been - and remains - very tepid. The question naturally arises of why the level of ambition of any proposed negotiations on trade facilitation in services should be so narrowly drawn and limited.

Further, even if governments insisted for political reasons on not undertaking any commitment to reduce the trade costs imposed by _discriminatory_ trade barriers, policy makers could at least consider undertaking the commitment of _status quo_ bindings regarding discriminatory conduct. If governments are genuinely committed to facilitating trade in services, they should at least consider not worsening the already restrictive level of discriminatory barriers
|Switzerland<br>Türkiye|Ethiopia<br>French Polynesia|Sri Lanka<br>St. Kitts and Nevis|
|---|---|---|
|United Kingdom|Gabon|Uganda|
|Uruguay|Ghana<br>Guatemala<br>Guinea|Vanuatu<br>Vietnam|

Note: * = No time-varying patterns in sector targeting, and so cannot be included in treatment group.

Table 4 then provides a breakdown of the FDI statistics for this country-sample, showing the total count per country and their number of included sectors. It also shows the unique country pairs (that is – the number of countries reporting their FDI position in the host country) which range from a low of 16 (for Uruguay) to a high of 29 countries (for Austria, the Russian Federation, and Switzerland).

To consider the share of FDI captured by this new sectoral FDI database, we also compare it to the aggregate FDI stock from the countries included in the World Bank’s harmonized bilateral FDI database.<sup>5</sup> This finds that the FDI-reporting countries jointly make up almost two-thirds of all global FDI stock. For the study sample this share is even higher, covering over 70 percent of all countries’ FDI stock (see Annex tables A1 and A2). The three countries with the highest share of FDI covered by our sectoral FDI database are Italy, the Arab Republic of Egypt and Finland (with 96, 95 and 95 percent of FDI covered by the sample, respectively) while the lowest countries are Hong Kong SAR, China, India and Uruguay (at 13, 44 and 50 percent, respectively). In sum, for most target countries the sectoral FDI database provides a reasonable approximation for their aggregate FDI stock. Yet, for selected countries the interpretation is more limited, and focused on only the effectiveness of IPAs at attracting FDI from OECD countries.

**Table 4: Study sample – breakdown by country*
agricultural production data). We do not find evidence of differential attrition of sample plots due to household attrition or plots transacted to other farmers that we did not track, however we do find access to irrigation causes an additional 6.4 - 10.2pp of plots to be rented out to a commercial farmer. We interpret the lack of data on these plots as biasing our primary estimates of the impacts of irrigation downwards, as these plots are cultivated with productive export crops, and we discuss attrition further in Appendix F.

# **2.3 Stylized facts**

To motivate our analysis of the impacts of hillside irrigation, we first introduce some stylized facts about irrigation in this context. Table 1 presents summary statistics for agricultural production from our four years of data, pooled across seasons.

12
0.81|1.00|0.97|0.31|
|Kenya|1.00|1.00|0.99||
|Lesotho|0.79|1.00|||
|Madagascar|0.93||0.92||
|Malawi|0.62|1.00|0.92||
|Mali|0.79|0.95|||
|Mozambique|0.87|1.00||0.31|
|Namibia|1.00|0.97|||
|Niger|0.44|0.47|0.55||
|Nigeria|0.44|0.32|0.97||
|Rwanda|0.88|1.00||0.01|
|Senegal|1.00|0.35|1.00||
|South Africa|0.84|0.72|1.00|0.41|
|Sudan|||||
|Tanzania|0.52|0.91|0.99||
|Uganda|1.00|1.00|0.20|0.02|
|Zambia|0.44|0.36|1.00||
|Zimbabwe||0.47|||
|**Average**|**0.78**|**0.82**|**0.87**|**0.29**|

_Source:_ Derived from Africa Infrastructure Country Diagnostic Power Tariff Database.

What becomes immediately clear is that some countries rank very high for cost recovery but do very poorly for equity and affordability and vice versa (table 11). Countries such as Chad, Mozambique, Rwanda, and Uganda tend to rank well for cost recovery but poorly for affordability and equity. On the other end, countries such as South
Tables 9 and 10 report the conditional factor demand functions for early season (i.e., preplanting and planting period) fertilizer and labor, respectively, the former estimated at both the intensive and extensive margins since there are many zero-valued observations.<sup>22</sup> The results highlight four intuitive findings. First, the provision of true plot size information has zero effect on fertilizer use reporting at the extensive margin. Farmers know whether they used fertilizer or not and that self-report is unaffected by corrective information about plot size. Fertilizer use, as a binary variable, is positively associated with plot size only and unrelated to either pre-treatment plot size measurement error or corrective information.

Second, the plot size information treatment significantly affects farmers' self-reported fertilizer use at the intensive margin, by roughly 7 percent of mean fertilizer use at mean plot size and pre-treatment measurement error (-0.298/4.244). Since the average farmer overestimates his plot size, corrective information on average told him that he was overestimating his area. This finding indicates that informational treatment induces farmers to reduce their estimates of fertilizer use intensity, too. Since farmers were asked to report their fertilizer use minutes after they witnessed the GPS measurement of their plot and were told the true plot size and the measurement error in their self-report of plot area, there was no opportunity for any actual adjustment in fertilizer use. These are pure spillover effects on beliefs, or at least on self-reports, caused by corrective information on a related but different variable. This raises concerns about the quality of selfreported data on fertilizer and labor inputs in agricultural household surveys, an issue that has received limited attention in the evolving discussion of improved household survey methods. NCME in non-land inputs may affect inferences about the determinants of and marginal returns to inputs (e.g., Abay, 2020).

Third, the treatment effects are systematically heterogeneous, varying especially with plot size. Farmers owning larger plots adjusted their self-reported fertilizer use intensity downwards by a larger
sample. In Table 1, it relies on comparing outcomes between observations in cells D and F with observations in cells E and G.<sup>19</sup> We include sampling weights to ensure results are representative of the population of cash transfer beneficiaries.

Second, we compare outcomes between households that are non-beneficiaries of cash transfers in villages assigned or not to BCC. We obtain estimates of BCC local spill-overs based on the following regression: This specification relies on comparing outcomes between observations in cells B and C in Table 1. We include sampling weights to ensure results are representative of the population of non-beneficiaries in cash transfer villages.

In addition to reporting robust (White-Huber) clustered standard errors and related asymptotic p-values for coefficients in equations (1) and (2), we also report the exact p values from a randomization-t test. Following Young (2018), the exact p-values are obtained from 2,000 simulations and take into account the stratified randomization.<sup>20</sup> While in principle the exact p-values could be more conservative since our design involves clustered randomization, the size of the experiment is not small and in practice the exact p values are close to the asymptotic p values. We also report joint test of significance of treatment effects based on Young (2018).

# _<u>4.2 Impacts of Cash Transfers</u>_

The study is also designed to assess the relative effect of the behavioral change component and cash transfers in improving parenting practices and children’s human capital. We can estimate the relative impacts of the two interventions on predicted beneficiary households based on baseline data.

As discussed above, the registry census and targeting data collection took place in the treatment groups. However, the baseline survey included all the variables necessary to estimate the proxy-means targeting score for all households in the baseline sample. On that basis, we can replicate the targeting process and

> 19 We also provide a robustness check by considering actual beneficiaries from the baseline sample only