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«ABSTRACT We present evidence that financing frictions adversely impact investment in workplace safety, with implications for worker welfare and ...»

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If more cash flow results in fewer injuries, β should be negative in the AJCA and oil experiments and positive in the financial crisis experiment. Motivated by the relation between injury rates and leverage documented in the previous section, we also run regressions where we include the interaction of Debt/Assets with Exposure ∗ T reatment in the AJCA and oil experiments to see if the sensitivity of injury rates to cash flow shocks is stronger in firms with more debt.19 For the AJCA experiment, we restrict the sample to the two years before and after implementation of the AJCA (2002 to 2003 and 2005 to 2006) to focus on changes around the shock. We set T reatment to one for observations in 2005 and 2006 and to zero for 20 observations in 2002 and 2003. We set Exposure to one if the sum of an establishment’s parent-firm foreign profits (Compustat variable pifo) from 2001 through 2003 is positive and zero otherwise.20 For the financial crisis experiment, we restrict the sample to 2006 to 2008 to focus on the period around the onset of the crisis.21 We set T reatment to one for observations in 2008 and to zero for observations in 2006 and 2007. Following the approach of Almeida et al. (2012), we constrain our sample to firms with 2007 fiscal year-ends between September 2007 and January 2008, as firms with earlier 2007 fiscal year-ends could have altered their maturity structures before the crisis began.22 For each firm, we define DebtDueIn1Y ear/Assets as debt maturing within one year (Compustat dd1) as of fiscal year-end 2007 divided by total assets. We then set Exposure to one if the parent firm’s DebtDueIn1Y ear/Assets is at or above the 75th percentile for the sample (0.0304) and zero otherwise. This cutoff is arbitrary, but the results are not sensitive to the choice of cutoff.

We use the full sample period for the oil price experiment, as oil prices moves continuously throughout this period. We set T reatment equal to the natural log of the average oil price in a given year as reported by the U.S. Energy Information Agency. We set Exposure to one if an establishment’s parent firm is involved in oil and gas extraction and zero otherwise.

We classify a firm as being in the oil and gas extraction business if it has an establishment in two-digit SIC code 13 (Oil and Gas Extraction) in the SOII at any time during the sample period or if it is classified by Capital IQ as being in the oil, gas, and consumable fuels business, excluding coal mining. We then remove establishments with a two-digit SIC code 13 from the sample.23 Panel A of Table VII summarizes the characteristics of treated and untreated establishments prior to treatment (since there is no pre-treatment period in the oil experiment, the characteristics for the first year an establishment appears in the sample are shown instead).

Two features are worth noting. First, while the treated group is reasonably large in the 21 AJCA and financial crisis experiments, there are only 150 treated establishments (belonging to only 19 firms) in the oil price experiment. This raises concerns about the external validity of the oil price experiment. Second, in all three experiments, treated and untreated establishments differ substantially on observable dimensions.

— Insert Table VII here — To minimize these differences, in each experiment we match each treated establishment to an untreated “control” establishment using propensity score matching. In the case of the AJCA and financial crisis experiments, we estimate a probit model where the dependent variable is Exposure and the explanatory variables are the regressors from Table V, using only the last observation for each establishment prior to the treatment year. We then fit the probit regression to estimate the propensity to be exposed, and match each treated establishment to the untreated establishment with the closest propensity.24 We do the same in the case of the oil experiment, except that we use the first observation for each establishment in the sample period for matching because of the lack of a pre-treatment period.

Panel B of Table VII presents summary statistics for treated and matched control establishments in each experiment. The matching process is successful at eliminating differences in observable characteristics in the AJCA and oil experiments. This is important, as the validity of our difference-in-differences approach depends on assignment to treated and control groups being as if random, conditional on observables. While we cannot rule out the possibility that the two groups in these experiments differ on unobservable dimensions, we take comfort in the fact that they are similar on observable dimensions. Matching is less successful at eliminating differences in the financial crisis experiment, raising concerns about nonrandom assignment in this experiment. We return to this issue shortly.

Panel C presents the broad industry breakdown of establishments in the treated and control groups for the AJCA and financial crisis experiments.25 Differences in industry composition are modest in the AJCA experiment but substantial in the financial crisis experiment.

These differences raise further concerns about nonrandom assignment.26 Another assumption underlying difference-in-differences estimation is that there are no differences in pre-treatment trends in the outcome variable in treated and untreated establishments. For the AJCA and financial crisis experiments, we assess the validity of this “parallel trends” assumption by plotting the portion of injury rates not explained by other observable variables for treated and control establishments over time. To do so, we estimate equation (2), omitting the interaction of T reatment and Exposure as well as the fixed effects. Figures 3 and 4 plot the annual mean of these residuals from the regression for treated and control establishments in the AJCA and financial crisis experiments, respectively.

— Insert Figures 3 and 4 here — While pre-treatment trends are almost identical in the AJCA experiment, they differ markedly in the financial crisis experiment, raising further concerns about the validity of this experiment — we return to this issue shortly as well. While there is no pre-treatment period in the oil experiment with which to assess validity of the parallel trends assumption (oil prices change every year), oil prices changed minimally from 2001, the year before the start of our sample period, to 2002 (from $21.84 to $22.51 per barrel). Over the same year, residual injury rates changed from -0.0048 in 2001 to -0.0047 in 2002 for treated establishments and from -0.0014 to -0.0016 for untreated establishments. The difference in change across the two groups is less than 1/10 of the mean absolute difference in annual change over the sample period, providing support for satisfaction of the parallel trends assumption in the oil experiment.27 Table VIII presents the difference-in-differences estimates for each of the three experiments (the first three columns), as well as the triple difference estimates involving leverage in the AJCA and oil experiments (the last two columns). Panels A and B present estimates 23 for OLS and Poisson models, respectively. The results are consistent across both classes of models and across all three experiments. The coefficients on T reatment ∗ Exposure in the first three columns are all consistent with an establishment’s injury rate falling (rising) after its parent firm receives a positive (negative) cash flow shock. The coefficients on the triple interaction terms in the last two columns are consistent with these responses being stronger in more indebted firms. These coefficients are all statistically significant at the 10% level or better.

— Insert Table VIII here — As these experiments involve cash flow shocks, we interpret the economic magnitudes implied by the coefficients on T reatment ∗ Exposure in the first three columns of Panel A in terms of the implied effect of a one-standard-deviation shock to a firm’s CashF low/Assets.

Because we do not observe the size of the actual cash flow shocks involved in these experiments, we must estimate them. Our estimates of economic magnitudes should therefore be interpreted cautiously.

From Table II, the sample standard deviation of CashF low/Assets is 0.146. Mean threeyear cumulative foreign profits as a fraction of assets for treated establishments is 0.0406.

Assuming that these profits are available for firms to invest domestically after the AJCA, they represent 27.8% of a one-standard-deviation cash flow shock. The coefficient of -0.0006 on T reatment ∗ Exposure in column (1) then implies that Injuries/Hour decreases by

0.0022 following a one-standard-deviation increase in total cash flow, which represents an 8.7% decrease relative to the mean Injuries/Hour of 0.0247.

Mean DebtDueIn1Y ear/Assets is 0.0584 for treated establishments and 0.0138 for control establishments. Assuming that no debt could be rolled over in 2008, treated establishments in the financial crisis experiment suffered a cash flow shock scaled by assets of

0.0446 relative to nontreated establishments. This shock represents 30.5% of a one-standarddeviation change in CashF low/Assetes. The coefficient of 0.0007 in column (3) then implies that Injuries/Hour increases by 0.0030 following a one-standard-deviation decrease in total cash flow, which represents an 11.9% increase relative to mean Injuries/Hour.

To assess the economic magnitude implied by the coefficient on T reatment ∗ Exposure in the oil price experiment, we first regress CashF low/Assets on annual log oil price for sample firms in the oil business, controlling for firm fixed effects. The coefficient on log oil price in this regression is 0.056, which is statistically significant at the 1% level. This point estimate, which represents the expected increase in CashF low/Assets associated with a oneunit increase in log oil price, is 38.4% of the standard deviation of CashF low/Assets. Thus, the coefficient of -0.0008 on T reatment∗Exposure in column (4) implies that a one-standarddeviation increase in CashF low/Assets is associated with a decrease in Injuries/Hour of 0.0021, or 8.4% relative to mean Injuries/Hour.

Panels C and D repeat the regressions in Panels A and B, substituting DAF W Injuries/Hour and DAF W Injuries, respectively, as the dependent variables. One note here is that the statistical power of these tests is likely to be low given the combination of the small sample sizes in the experiments and the relative infrequency of days-away-from-work injuries. The results are consistent with those in Panels A and B, though only three of the five coefficients of interest in Panel C and two of the five in Panel D are statistically significant. Nevertheless, the table provides at least some evidence that it is not only less serious injuries that decrease (increase) following positive (negative) cash flow shocks.

As noted previously, treated and control establishments differ markedly on observable characteristics in the financial crisis experiment, and the parallel trends assumption appears unlikely to be satisfied in this experiment. To further address these concerns, we next match treated and control establishments on observable characteristics one-at-a-time as well as on the pre-treatment injury rate trend separately and reestimate the Poisson model for each resulting matched sample. We match on pre-treatment trends by computing the pre-treatment

–  –  –

The first three columns show that the matching exercise is successful at eliminating differences in each given characteristic. The final two columns show that the coefficient on the interaction of Crisis and HighDebtDue is positive in all of the regressions, and is statistically significant in all but one. This finding provides some comfort that the financial crisis results are not driven by differences in any single observable characteristic.

V. Firm Value and Injury Rates

In this section, we consider the implications of the results in Sections III and IV for optimal financial policy. If firms bear costs from an elevated workplace injury risk, then our results suggest a previously undocumented cost of financial policies, such as high leverage, that increase the likelihood that financing constraints bind in the future. Firms may bear such costs directly through higher health insurance costs, increased downtime, lower productivity, and compensable lawsuits, as well as indirectly through compensating wage differentials that employees demand for exposure to injury risk. To our knowledge, there are no existing estimates of the total costs to a firm of greater injury risk.

We attempt to estimate these costs by examining the relationship between firm value and injury rates at a firm’s establishments. We do so by regressing a firm’s Tobin’s Q on its prior year’s injury rate, controlling for a number of firm-level observable characteristics as well as firm and year fixed effects. One challenge is that we observe injuries at the establishment rather than the firm level. To compute a firm-level injury rate for a given year, we add up 26 injuries at all establishments in the BLS data belonging to a firm during the year, and divide this figure by the sum of hours worked at those establishments during the year. We multiply this quotient by 1,000 to make the numbers easier to interpret. We refer to the resulting variable, measured in the prior year, as LaggedInjuries/Hour. This is a crude measure of the firm-level injury rate, as establishments participating in the BLS’ survey change from year to year. We exclude any establishment appearing in the data only once during our sample period to reduce this noise.28 Table X presents the regression results. Columns (1) and (2) report estimates of the sensitivity of Q to lagged injury rate without and with firm-level control variables, respectively. The coefficients on LaggedInjuries/Hour are negative and statistically significant at the 5% level. This is consistent with firms bearing costs from greater injury risk. We are cautious, however, about ascribing causality to this relationship. Despite the inclusion of firm fixed effects and controls in the regressions, it is difficult to rule out the possibility that some omitted variable drives the relation. For example, poorly managed companies are likely to have both high injury rates and low value. We attempt to address these concerns at least in part by examining the lead-lag structure of the relationship between Q and injury rate.

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