{"component": "clause", "props": {"groups": [{"snippet": "This paper focuses on explaining the degree of access that interest groups obtain to public officials. However, access can be conceptualized as a two-step process in which first interest groups gain access, and, subsequently, they can have repeated access. This section evaluates the robustness of the results while accounting for those organizations without access. More specifically, Table 4.3 below presents the results of hurdle negative binomial models, a two- step method that first assesses the probability of obtaining the binary outcome, in this case obtaining access or not, and subsequently calculates the effects of the same explanatory factors on the level of access (see \u2587\u2587\u2587\u2587\u2587\u2587 et al. 2019 for a similar approach). This model is appropriate in the case of a sequential decision-making process. Even though the two stages of granting access once and deciding to grant access multiple times are estimated separately, the second stage should be interpreted as conditional on the first stage. Prioritizing Professionals? The first step of the model (binary logit), shows that organizational capacity increases the likelihood of gaining access. In contrast, member involvement and functioning as a transmission belt is not related to the probability of gaining access.31 That is, the same organizational factors that explain the level of access seem to explain the likelihood of gaining access. Additionally, the second step of the model (zero-truncated negative bi- nomial) confirm the results presented in Table 4.2. The only differences are found in the significance levels of some control variables. More specifically, the second step of hurdle models show that only organizational scale and resources are significantly related to the degree of access, yet this result is not consistent across all model specifications in Table", "snippet_links": [{"key": "public-officials", "type": "clause", "offset": [85, 101]}, {"key": "step-process", "type": "clause", "offset": [150, 162]}, {"key": "gain-access", "type": "definition", "offset": [194, 205]}, {"key": "accounting-for", "type": "clause", "offset": [316, 330]}, {"key": "more-specifically", "type": "clause", "offset": [367, 384]}, {"key": "step-method", "type": "clause", "offset": [466, 477]}, {"key": "level-of-access", "type": "clause", "offset": [664, 679]}, {"key": "see-\u2587", "type": "clause", "offset": [681, 686]}, {"key": "in-the-case", "type": "clause", "offset": [755, 766]}, {"key": "granting-access", "type": "clause", "offset": [838, 853]}, {"key": "to-grant-access", "type": "clause", "offset": [872, 887]}, {"key": "second-stage", "type": "definition", "offset": [933, 945]}, {"key": "first-stage", "type": "definition", "offset": [990, 1001]}, {"key": "first-step", "type": "clause", "offset": [1035, 1045]}, {"key": "the-model", "type": "clause", "offset": [1049, 1058]}, {"key": "capacity-increases", "type": "clause", "offset": [1101, 1119]}, {"key": "member-involvement", "type": "clause", "offset": [1167, 1185]}, {"key": "related-to", "type": "clause", "offset": [1232, 1242]}, {"key": "organizational-factors", "type": "clause", "offset": [1298, 1320]}, {"key": "second-step", "type": "clause", "offset": [1422, 1433]}, {"key": "significance-levels", "type": "definition", "offset": [1566, 1585]}, {"key": "control-variables", "type": "clause", "offset": [1594, 1611]}], "samples": [{"hash": "6EqJeFB4TvX", "uri": "/contracts/6EqJeFB4TvX#robustness-checks", "label": "License Agreement", "score": 29.2757034302, "published": true}, {"hash": "h4SCVs4iIGf", "uri": "/contracts/h4SCVs4iIGf#robustness-checks", "label": "License Agreement", "score": 23.8138256073, "published": true}], "size": 2, "hash": "cc6053ec35112afc64e620ec8f020a4d", "id": 1}, {"snippet": "As reported in Tables 5 and 6, I re-estimated the models by including market orientation and cross-functional integration as control variables to ensure that CBM effect was still significant after controlling for those two related conditions. H1a and b and the results for the interactions are consistent with the results of the analysis without these control variables. Moreover, the incremental R2 explained by adding CBM to models that included market orientation and cross functional integration, respectively, is statistically significant at p<0.05 in the sales growth and employee engagement models indicating that a CBM measure that focuses on internal and community constituencies explains variance over and above these two established variables9. To examine persistence and proxy for omitted variables, I included the lag dependent variable in the sales growth model, in addition to the firm and country level controls. The pattern of results remained largely stable to this addition. In order to verify that the choice of the estimation approach did not bias the results, I also re-estimated the four recursive equations utilizing Roodman\u2019s (2009) conditional mixed process 9 The effect of the CBM measure that includes market constituents however becomes weaker when market orientation is added to the model and in some cases becomes insignificant.", "snippet_links": [{"key": "control-variables", "type": "clause", "offset": [125, 142]}, {"key": "to-ensure", "type": "clause", "offset": [143, 152]}, {"key": "related-conditions", "type": "definition", "offset": [223, 241]}, {"key": "consistent-with-the", "type": "clause", "offset": [294, 313]}, {"key": "results-of-the", "type": "clause", "offset": [314, 328]}, {"key": "statistically-significant", "type": "definition", "offset": [518, 543]}, {"key": "sales-growth", "type": "definition", "offset": [561, 573]}, {"key": "employee-engagement", "type": "clause", "offset": [578, 597]}, {"key": "dependent-variable", "type": "clause", "offset": [831, 849]}, {"key": "the-firm", "type": "clause", "offset": [892, 900]}, {"key": "the-pattern", "type": "clause", "offset": [929, 940]}, {"key": "to-verify", "type": "definition", "offset": [1003, 1012]}, {"key": "effect-of-the", "type": "clause", "offset": [1190, 1203]}, {"key": "the-model", "type": "clause", "offset": [1309, 1318]}], "samples": [{"hash": "2YDCYoiPruI", "uri": "/contracts/2YDCYoiPruI#robustness-checks", "label": "Distribution Agreement", "score": 21.2829647064, "published": true}], "size": 2, "hash": "b40f140e5ad6d92354b2cafc99b7c653", "id": 2}, {"snippet": "4.1. Tail risk connectedness in different market conditions\n4.2. The connectedness at different tail risk levels\n4.3. Business linkages and tail risk spillovers between closely-linked industries\n4.4. Business linkages and tail risk spillovers between nonfinancial industries", "snippet_links": [{"key": "tail-risk", "type": "definition", "offset": [5, 14]}, {"key": "market-conditions", "type": "definition", "offset": [42, 59]}, {"key": "risk-levels", "type": "clause", "offset": [101, 112]}], "samples": [{"hash": "foAabNP4idO", "uri": "/contracts/foAabNP4idO#robustness-checks", "label": "Research Paper", "score": 27.830953598, "published": true}], "size": 2, "hash": "bbd4671934697ce090dd36fd422e66e5", "id": 3}, {"snippet": "Private protection rackets are famously \u2587\u2587\u2587\u2587 in Russia and Ukraine, though they are less active in the other post-communist countries. In a survey of Russian shopkeepers by \u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587 and \u2587\u2587\u2587\u2587 (1998), 33% reported that one of the roles of private protection organizations was to enforce agreements (though far more reported their role was to \u201cprotect\u201d the shopkeepers from other criminals). According to anecdotes, though, the mafia plays a larger role with shops than with manufacturing firms of the sort we surveyed. Firms reporting disputes with trading partners were asked whether \u201can informal private agency specializing in such cases\u201d aided in the resolution of the dispute. Only 5% of firms gave this response, though 48% of Russian firms and 26% of Ukrainian firms reporting disputes said they used such an agency. We create two variables that provide some control for the availability of private enforcement. When added to the basic regression reported in column 3, neither \u201cother third party enforcement\u201d (\u03b2=2.01, t=0.52) nor using \u201can informal private agency specializing in such cases\u201d (\u03b2=-8.95, t=1.25) has a significant effect on credit. Their inclusion has almost no effect on the relational contracting variables or on the courts variable. The results shown on Table 3 are also robust to modifications in the sample criteria. All of the reported coefficients remain significant and of close to the same magnitude when relationships and/or firms started more than 10 years before the survey -- prior to the beginning of economic reforms -- are excluded from the sample. The results are similarly robust to limiting the sample to the three Eastern European countries. Including state-owned and export customers also has only modest effects. A regression with state enterprises and export customers is shown in Appendix B, along with separate regressions for each country. (Russia and Ukraine are combine because of the small sample sizes in these countries.) Courts are positively associated with credit in each of the country level regressions, though the effect is significant only in Slovakia.22 With the exception of social networks in Poland, the information network variables also have the right sign everywhere, and are significant most of the time.", "snippet_links": [{"key": "in-russia", "type": "clause", "offset": [45, 54]}, {"key": "other-post", "type": "clause", "offset": [103, 113]}, {"key": "according-to", "type": "definition", "offset": [392, 404]}, {"key": "trading-partners", "type": "clause", "offset": [550, 566]}, {"key": "private-agency", "type": "definition", "offset": [599, 613]}, {"key": "in-such-cases", "type": "clause", "offset": [627, 640]}, {"key": "the-dispute", "type": "clause", "offset": [669, 680]}, {"key": "an-agency", "type": "clause", "offset": [813, 822]}, {"key": "availability-of", "type": "clause", "offset": [882, 897]}, {"key": "column-3", "type": "definition", "offset": [966, 974]}, {"key": "third-party-enforcement", "type": "clause", "offset": [991, 1014]}, {"key": "significant-effect", "type": "definition", "offset": [1123, 1141]}, {"key": "effect-on-the", "type": "clause", "offset": [1183, 1196]}, {"key": "table-3", "type": "clause", "offset": [1278, 1285]}, {"key": "close-to", "type": "definition", "offset": [1402, 1410]}, {"key": "the-survey", "type": "clause", "offset": [1496, 1506]}, {"key": "prior-to-the", "type": "clause", "offset": [1510, 1522]}, {"key": "beginning-of", "type": "clause", "offset": [1523, 1535]}, {"key": "european-countries", "type": "definition", "offset": [1663, 1681]}, {"key": "state-enterprises", "type": "definition", "offset": [1774, 1791]}, {"key": "appendix-b", "type": "definition", "offset": [1825, 1835]}, {"key": "associated-with", "type": "definition", "offset": [1996, 2011]}, {"key": "the-country", "type": "definition", "offset": [2030, 2041]}, {"key": "with-the-exception-of", "type": "clause", "offset": [2114, 2135]}, {"key": "social-networks", "type": "clause", "offset": [2136, 2151]}, {"key": "information-network", "type": "clause", "offset": [2167, 2186]}, {"key": "the-right", "type": "clause", "offset": [2207, 2216]}], "samples": [{"hash": "8n6I6A0PMmw", "uri": "/contracts/8n6I6A0PMmw#robustness-checks", "label": "Courts and Relational Contracts", "score": 19.0, "published": true}], "size": 1, "hash": "60838768f7d8f4938287fd2edbedf628", "id": 4}, {"snippet": "Earlier findings that link experience with risk taking could be driven by the fact that there is an inverse correlation between Tracking Error and market capitalization of a fund\u2019s holdings. That is, all other things being equal, a large cap fund has lower Tracking Error than a small cap fund. Furthermore, given that junior managers manage smaller funds, on average, we would expect more Tracking Error for junior managers simply because they manage smaller funds. In order to alleviate these concerns, I divide all funds into two groups based on Morningstar\u2019s categorization of fund size capitalization. Using Morn- ingstar Category grouping, I run the same regressions for risk taking by experience for large and mid/small cap funds separately. Results are reported in Table 11. In Table 11, I again find results consistent with my findings in Table 9 for all fund size groups. Funds managed by junior fund managers take significantly more risk when com- pared to their seasoned counterparts for the more recent period. The results for the earlier period are also consistent throughout the fund size group with earlier finding. With these results, I show that my findings of the relationship between risk taking and experience are robust to the negative correlation between Tracking Error and fund market capitalization. Next, I use other measures of risk taking to test whether my finding is robust to the choice of measuring risk in Table 12. The first alternative measure I use is Amihud and Goyenko (2013) R2 (AG Rsq). I regress the future twelve months of monthly fund excess return over the one month T-\u2587\u2587\u2587\u2587 rate on \u2587\u2587\u2587\u2587-\u2587\u2587\u2587\u2587\u2587\u2587-\u2587\u2587\u2587\u2587\u2587\u2587\u2587 4 Factor return to get the R2. As I noted previously, since a high R2 implies lower risk taking/selectivity, I subtract the R2 measure from one to be in accordance with other measures that capture risk taking. The R2 measure has the benefit of not having to know or define the specific benchmark each mutual fund is using and thus is able to successfully detect funds that are truly active in picking stocks against funds that invest in multiple index funds and hide under the radar of other active management measures. The results of the first two specifications show the consistent result that junior fund managers take more risk in the more recent period compared to their seasoned counterparts when AG Rsq is used. The next two measures are based on the holdings of each mutual fund. In order to use holdings-based measures, it is necessary that I construct a map between the Morningstar, CRSP and Thomson databases. I follow the methodology provided in \u2587\u2587\u2587\u2587 and Van Binsbergen (2015) and Pa\u00b4stor, \u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587, and \u2587\u2587\u2587\u2587\u2587\u2587 (2015) in mapping between Morningstar and CRSP Mutual Fund Database. In a nutshell, I independently map CRSP MFDB to Morningstar Principia CDs and then Morningstar Direct to Morningstar Principia CDs. I used monthly returns, TNA, CUSIP, Ticker, fund names, and dividends to map the datasets. In the end, I was able to map 90.2%of fund-month observations in Morningstar to CRSP Mutual Fund Database. Then, I use MFLINKS from \u2587\u2587\u2587\u2587\u2587\u2587\u2587 Research Data Services (WRDS) to map Morningstar Data to Thomson mutual fund holdings database. I randomly select funds from my mapping and verify that my mapping is robust. The second alternative measure of risk taking is Return Gap as suggested by Kacper- czyk et al. (2008). Return Gap captures unobserved actions of mutual fund managers and is measured by the difference between actual fund return and hypothetical fund return based on aggregated past reported holdings. I use the average of future 3 month Return Gap measures in order to test if junior fund managers take more unobserved actions. The next two specifications show that junior fund managers take more risk in the more recent period compared to their seasoned counterparts. The third alternative measure of risk taking is Active Share from \u2587\u2587\u2587\u2587\u2587\u2587\u2587 and \u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587 (2009). Active Share is measured by the differ- ence in holdings compared to their benchmark index at a certain point in time when mutual funds report their holdings to the SEC. I follow the specification in their paper in explaining Active Share and add manager-specific dummy variables that are of interest to my project, such as CFA, MBA, and Female. In \u2587\u2587\u2587\u2587\u2587\u2587\u2587 and Petajisto (2009), they show that past Tracking Error is most closely related to Active Share measure and also include Log Size2 to take into account the nonlinear effect of fund size on risk taking. Consistent with their finding, I find that Tracking Error has the largest economic magnitude in explaining the Active Share and that these two variables are positively correlated with each other. Also, I again find that junior fund managers take more risk in the more recent period. On the other hand, for the earlier period, the results are not statistically significant. This could be due to the fact that while the risk taking incentives favor the seasoned managers during this period, the difference in those incentives between seasoned and junior fund managers subjective judgment, resulting in potential bias. In Table 14, I run the same analysis as in Table 9 analyzing the relationship between risk taking and experience. Industry experience is the number of years each fund manager worked in the investment industry and Industry Exp Group is a categorical variable that equals 1 for the inexperienced group and 2 for the experienced group based on median value of each cross sectional industry experience. Industry Middle is a dummy variable that equals 1 if a fund manager\u2019s industry experience is between the 40th to 60th percentile of each cross section and 0 otherwise. Industry Seasoned is a dummy variable that equals 1 if a fund manager\u2019s industry experience is in the top 40th percentile in each cross section and 0 otherwise. Throughout all specifications, I find consistent results with earlier tables that junior fund managers take more risk in the more recent period compared to seasoned fund managers and that seasoned fund managers take more risk compared to junior fund managers in the earlier period. With this finding, I provide evidence that fund manager age works as a good proxy for manager experience in the mutual fund industry.", "snippet_links": [{"key": "the-fact", "type": "clause", "offset": [74, 82]}, {"key": "tracking-error", "type": "clause", "offset": [128, 142]}, {"key": "market-capitalization", "type": "definition", "offset": [147, 168]}, {"key": "given-that", "type": "clause", "offset": [308, 318]}, {"key": "in-order-to", "type": "clause", "offset": [467, 478]}, {"key": "all-funds", "type": "clause", "offset": [514, 523]}, {"key": "based-on", "type": "clause", "offset": [540, 548]}, {"key": "fund-size", "type": "definition", "offset": [581, 590]}, {"key": "table-11", "type": "clause", "offset": [773, 781]}, {"key": "consistent-with", "type": "clause", "offset": [817, 832]}, {"key": "table-9", "type": "definition", "offset": [848, 855]}, {"key": "funds-managed", "type": "definition", "offset": [882, 895]}, {"key": "fund-managers", "type": "definition", "offset": [906, 919]}, {"key": "the-fund", "type": "clause", "offset": [1090, 1098]}, {"key": "relationship-between", "type": "clause", "offset": [1183, 1203]}, {"key": "other-measures", "type": "clause", "offset": [1337, 1351]}, {"key": "risk-in", "type": "clause", "offset": [1431, 1438]}, {"key": "table-12", "type": "definition", "offset": [1439, 1447]}, {"key": "the-future", "type": "clause", "offset": [1537, 1547]}, {"key": "twelve-months", "type": "definition", "offset": [1548, 1561]}, {"key": "excess-return", "type": "clause", "offset": [1578, 1591]}, {"key": "one-month", "type": "definition", "offset": [1601, 1610]}, {"key": "return-to", "type": "definition", "offset": [1655, 1664]}, {"key": "in-accordance-with", "type": "clause", "offset": [1796, 1814]}, {"key": "the-benefit", "type": "clause", "offset": [1875, 1886]}, {"key": "invest-in", "type": "clause", "offset": [2073, 2082]}, {"key": "index-funds", "type": "clause", "offset": [2092, 2103]}, {"key": "management-measures", "type": "clause", "offset": [2145, 2164]}, {"key": "results-of-the", "type": "clause", "offset": [2170, 2184]}, {"key": "in-\u2587", "type": "clause", "offset": [2601, 2605]}, {"key": "monthly-returns", "type": "clause", "offset": [2878, 2893]}, {"key": "fund-names", "type": "clause", "offset": [2915, 2925]}, {"key": "data-services", "type": "definition", "offset": [3111, 3124]}, {"key": "fund-holdings", "type": "clause", "offset": [3174, 3187]}, {"key": "fund-return", "type": "definition", "offset": [3492, 3503]}, {"key": "benchmark-index", "type": "definition", "offset": [4016, 4031]}, {"key": "in-time", "type": "definition", "offset": [4051, 4058]}, {"key": "mutual-funds", "type": "clause", "offset": [4064, 4076]}, {"key": "the-sec", "type": "definition", "offset": [4102, 4109]}, {"key": "the-specification", "type": "clause", "offset": [4120, 4137]}, {"key": "related-to", "type": "clause", "offset": [4371, 4381]}, {"key": "take-into-account", "type": "definition", "offset": [4433, 4450]}, {"key": "effect-of", "type": "definition", "offset": [4465, 4474]}, {"key": "the-other-hand", "type": "clause", "offset": [4787, 4801]}, {"key": "statistically-significant", "type": "definition", "offset": [4847, 4872]}, {"key": "the-risk", "type": "definition", "offset": [4915, 4923]}, {"key": "table-14", "type": "clause", "offset": [5120, 5128]}, {"key": "industry-experience", "type": "clause", "offset": [5231, 5250]}, {"key": "number-of-years", "type": "clause", "offset": [5258, 5273]}, {"key": "the-investment", "type": "definition", "offset": [5302, 5316]}, {"key": "cross-section", "type": "definition", "offset": [5653, 5666]}, {"key": "the-mutual", "type": "definition", "offset": [6235, 6245]}], "samples": [{"hash": "4JBV0SS25PB", "uri": "/contracts/4JBV0SS25PB#robustness-checks", "label": "Distribution Agreement", "score": 26.4784889221, "published": true}], "size": 1, "hash": "f2ab092c2c27572437df46548dd19f41", "id": 5}, {"snippet": "Thus far, we have relied on bidder announcement returns to measure the effect of CEO home bias on the value of the firm. In this section, we discuss some potential econometric concerns with such an approach and provide a series of robustness checks which, by and large, confirm our main conclusions. Endogeneity is often a major concern in corporate finance studies. In our setting, causal interpretations of the coefficients of interest are only valid if, conditional on our other explanatory variables, the \u201cCEO home bias\u2019\u2019 is randomly assigned. To illustrate this omitted variable problem, suppose that birth rates are higher in exactly the same target states that, for whatever reason, are associated with value destroying acquisitions. In this case, our results could be driven by this omitted variable. In order to address this problem, we try to control for the joint distribution of acquirers and targets using simulations.14 To illustrate this approach, consider first the subsample of cross-state acquisitions. For each cross-state acquisition in which the CEO birth state was the same as the target state, we randomly choose another acquisition with the same bidder and target state but with different CEO birth state. This produces a sample in which the likelihood of a CEO home bias is fifty percent. Next, we run a regression of bidder announcement returns on the CEO home bias dummy and the controls described in Table 3. To prevent our results from being driven by this particular choice of control acquisitions, we repeat this process 1,000 times and use the distribution of coefficients to draw our statistical inferences. Table 9 presents the results using both the states (Panel A) and distances (Panel B) as our measure of birth region proximity. For brevity, we only report the empirical distributions and empirical p-values for the Home Bias coefficients. Consistent with our previous results, we find a negative and significant impact of home bias, but only for distant mergers. For example, in Panel A, the home bias coefficients for in state mergers are not statistically significant, and the economic magnitude is roughly 1/7th of the cross state mergers. The results for distance-based home bias mergers in Panel B are similar. Another potential problem with the interpretation of the coefficients in Table 3 is that our approach relies on bidder announcement returns, whereas it is possible that the market incorrectly assesses the relative merits of home bias mergers. In Table 10, we estimate the longer-term effects of CEO home bias on the value of the firm using a calendar time approach which is less susceptible to econometric issues (\u2587\u2587\u2587\u2587\u2587\u2587 and \u2587\u2587\u2587\u2587, 1997). The calendar time strategy involves buying each home bias merger beginning three days after the announcement and holding for 6, 12, and 24 months. We use the Fama-French 3- factor model to risk-adjust returns, and report the monthly alpha for the set of home bias mergers. To control for average post-merger performance, we also calculate 3-factor alpha for a randomly drawn set of matched non-home bias mergers based on the location and industry of the merged firms as in Table 9. Table 10 reports the average alpha for the 1000 simulated merger portfolios, as well as the empirical p-value that the merger portfolio underperforms the simulated portfolio. The evidence in Table 10 does not support the view that the initial negative reaction to distant home bias deals reflects misreaction. 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Neither the availability of other private third party enforcement (\u03b2= 0.03, t=0.45) nor the use of private enforcement in resolving the firm\u2019s most recent dispute (\u03b2= - 0.01, t=0.37) has a significant effect on the probability of rejecting and offer. The magnitude of the courts effect increases marginally to 7% when either of these are included in the regression. Using independent country and industry controls makes no difference to the results. As an alternative measure of the complexity of the input, we used the question regarding how long it would take the buyer to find alternative inputs if the seller failed to deliver. Longer replacement times imply more risk on the part of the buyer. The time to replace is correlated with both the production of inputs sold only to this buyer (\u03c1 = .20) and with having no alternative supplier (\u03c1 = .34). The time to replace is not significant when it is included with these other two variables, but is when it is used in place of these other variables. The measured effect of courts is not changed with the time to replace is added to the regression; the courts effect is somewhat larger (8%) when time to replace is used in place of the other two variables. Finally, we included measures of the frequency of ongoing visits by the supplier to the manufacturer and measures of the competitiveness of the buyer\u2019s market, and the proportion of the incumbent suppliers bill which the buyer pays with delay. Ongoing visits from the supplier to the customer are significantly associated with higher rates of rejection of the new supplier. One measure of competitive markets (the manager\u2019s estimate of demand elasticity) is significant and indicates that buyers in more competitive markets are more likely to reject the offer. Two measures of competitiveness\u2014the number of competitors located nearby and indication that the buyer prices its goods with reference to competitor\u2019s prices rather than through bargaining with the customer\u2014are not significant. Credit received from the existing supplier also has no significant effect. None of these variables has any effect on the estimated magnitude of the effect of courts. Excluding relationships and firms started more than ten years before the survey has no effect on the magnitude of the courts effect. Neither does limiting the sample to the three Eastern European countries. Including state-owned and import suppliers in the sample has no effect on the magnitude of courts, but increases the precision of the measurement somewhat (\u03b2= - 0.06, t = 2.97, see Appendix B). At the single country level, courts have a significant negative effect only in Slovakia. The measured effect of courts is very close to zero in Poland, though it is negative and close to significant when the Polish sample is limited to custom inputs (See Appendix B). Random effects and linear probability (OLS) regressions produce similar results on the key variables. The random effects regression with the same specification as column 1 results in an insignificant coefficient on written quality specifications and on the variable indication a relationship duration of 3 to 12 months. In the subsample of standard inputs (column 5 specification), both the linear probability and random effects regressions produce significant coefficients for the effectiveness of courts. However, the magnitude of the coefficient remains much small than in the subsample of custom inputs. 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I use \u2587\u2587\u2587\u2587\u2587\u2587\u2587 (1997) four factor adjusted excess return as the dependent variable with the full set of controls in these regressions. The results are reported in Table 2.9. Regression (1) and (2) report the value-weighted regression results with full set of con- trols. The weighting variable is firm\u2019s market capitalization at the beginning of each month. The regression coefficients now reflect the impacts for each dollar invested. Similar as the findings in the univariate portfolio sorts, the signs and statistical significance of LQP, UQP and DownAsy remain intact, but the economic magnitude of the impacts are reduced for LQP and DownAsy. Regression (3) and (4) report the regression results when the sample is restricted to NYSE stocks only. Since stocks listed on NYSE tend to be larger size stocks, the findings are similar to value-weighted results. Regression (5) and (6) report the regression results using non-overlapping yearly obser- vations. Using non-overlapping periods are less efficient statistically, but do not cause the returns to be autocorrelated, so the standard t-statistics are reported. The findings are almost the same as the results using overlapping periods, with only small changes to some coefficients.", "snippet_links": [{"key": "this-subsection", "type": "definition", "offset": [5, 20]}, {"key": "excess-return", "type": "clause", "offset": [278, 291]}, {"key": "dependent-variable", "type": "clause", "offset": [299, 317]}, {"key": "the-value", "type": "clause", "offset": [439, 448]}, {"key": "market-capitalization", "type": "definition", "offset": [539, 560]}, {"key": "beginning-of", "type": "clause", "offset": [568, 580]}, {"key": "signs-and", "type": "clause", "offset": [734, 743]}, {"key": "statistical-significance", "type": "definition", "offset": [744, 768]}, {"key": "to-value", "type": "definition", "offset": [1071, 1079]}, {"key": "using-non", "type": "clause", "offset": [1151, 1160]}, {"key": "overlapping-periods", "type": "clause", "offset": [1206, 1225]}, {"key": "the-standard", "type": "clause", "offset": [1314, 1326]}, {"key": "changes-to", "type": "clause", "offset": [1445, 1455]}], "samples": [{"hash": "5kHeqVYZJ9T", "uri": "/contracts/5kHeqVYZJ9T#robustness-checks", "label": "Distribution Agreement", "score": 24.1128311157, "published": true}], "size": 1, "hash": "722c1731743766be5f2a06afdc3a35ec", "id": 8}, {"snippet": "Adding Population as a Control to Hy- potheses 1 and 2 224 A.2.10 Weighting the Dependent Variables for Hypotheses 1 and 2 \u2587\u2587\u2587 \u2587.\u2587 \u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587 to Chapter 5 231 A.3.1 Different CAR Windows in OLS Regression 231 A.3.2 Reconceptualizing the Independent Variable: Any Private Prisons234", "snippet_links": [{"key": "dependent-variables", "type": "clause", "offset": [80, 99]}, {"key": "chapter-5", "type": "definition", "offset": [143, 152]}, {"key": "independent-variable", "type": "definition", "offset": [235, 255]}], "samples": [{"hash": "eoAgVX5j6pE", "uri": "/contracts/eoAgVX5j6pE#robustness-checks", "label": "Distribution Agreement", "score": 28.4247570038, "published": true}], "size": 1, "hash": "e6bb5a90086739598561de3613e35959", "id": 9}, {"snippet": "In this section we report the results of several robustness tests of our findings to alternative variable definitions and sample restrictions. In doing so, we build on the single-split specification (II) to 12Regression coefficients in probit models cannot be interpreted as simple slopes as in ordinary linear regressions, but have to be interpreted in terms of Z-scores (i.e. as changes in Z-score for one unit increase in the explanatory variable). consider all available observations and guarantee a sufficient number of observations for the different sample restrictions. First, Table 7 reports the results obtained from modifications of specification (II) aimed at ensuring a vertical-type connection between a firm\u2019s imported inputs and its core export product. In particular, columns (1) and (2) report the results when we restrict the sample to import transactions that are classified as intermediates or capital goods according to the Broad Economic Categories classification; columns (3) and (4) show the results when we use our alternative dependent variable (d integr IFEXihjt), which conditions the classification of transactions as intra-firm also on the existence of a firm\u2019s affiliate in the source country declaring intra-firm export activities. The results in Table 7 confirms those in Table 4: better IPR quality diminishes the propensity to integrate in relatively downstream stages for complements, while the impact for substitutes is not statistically significant. Moreover, the differences between complements and substitutes, in line with theoretical predictions, become more pronounced both with respect to inputs\u2019 upstreamness and relative knowledge intensity along the value chain. Specifically, the impact of Upstr remains significantly negative for complements, while it becomes significantly positive for substitutes in column (2); the interaction between lnIPR and Upstr becomes significantly negative in column (2); and the impact of d knint downstr turns insignificant for complements in column (3), while remaining highly significant and positive for substitutes. Second, Table 8 presents the results obtained using two alternative indicators of sequential com- plements/substitutes described in Section 4.2. In particular, columns (1)-(4) use the indicator d complrho\u00d7alpha(ind.) based on the core product\u2019s demand elasticity rho (as a proxy for \u03c1) and the industry average of the \u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587\u2587 index (as a proxy for (inverse) \u03b1); columns (5-8) use in- stead the dummy d complrho\u2212alpha(elast.) based on the difference between rho and another proxy for \u03b1 based on the demand elasticity of imported intermediate and capital goods. Due to signifi- cant \u2018frailty\u2019 confirmed by the likelihood-ratio test, we continue to rely on a random effects probit estimator, thereby controlling for unobserved heterogeneity at detailed firm-country-product level. The results in Table 8 show that our previous findings reported in Table 4 are robust to the alternative ways of disentangling complements from substitutes. In the case of complements, in all columns the impact of better IPR quality is again significantly negative. Moreover, the interaction term of IPR quality with upstreamness is still positive and even more significant than before. Finally, the estimates also remain positive for the coefficient on the dummy d knint downstr, which indicates when knowledge intensive inputs are located more downstream along the value chain. On the other hand, no significant effect of IPR quality is detected in the case of substitutes. Further robustness checks can be found in Appendix B where, for both complements and sub- stitutes, we focus on the case of higher relative knowledge transmission upstream as this case is more readily comparable with the case of higher degree of upstream contractibility of tangible in- vestments. After presenting our baseline results for specification (III), we extend the analysis to alternative measures of sequential complements/substitutes. We then look at how our results vary across firms that differ in their reliance on inputs sourced by a single country. Finally, we control for additional source country institutional variables that could potentially influence our results in different parts of the value chain. 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