Is There a VA Advantage - Validity

Appendix A.1 IV Validity A.1.1 Exclusion Restriction Under the standard assumptions for IV validity in Imbens and Angrist (1994), ambulance companies would be subject to the exclusion restriction, in Condition 1(ii), that they only affect outcomes by whether they transport patients to the VA, and not by other treatments that they may administer during the ambulance ride or by their choice of non-VA hospitals. Following Kolesar et al. (2015), we relax this assumption to allow for differences in potential treatments and non-VA hospital choices across ambulance companies but require that such differences that may affect outcomes are not systematically related to ambulance propensity to transport to the VA. Specifically, we include controls C𝑖 that are related to actions by the ambulance after pickup in the first-stage and reduced-form relationships: 𝐷 𝑖 = 𝜋1 𝑍𝑖 + X0𝑖 𝛿1 + C𝑖 𝜂1 + 𝜁1,𝑧 (𝑖) + 𝜀 1,𝑖 ; 𝑌𝑖 = 𝜋2 𝑍𝑖 + X0𝑖 𝛿2 + C𝑖 𝜂2 + 𝜁2,𝑧 (𝑖) + 𝜀 2,𝑖 . Under each set of ambulance-related controls, we examine the stability of 𝛽ˆ𝐼 𝑉 = 𝜋ˆ 2 /𝜋ˆ 1 . We consider four sets of controls in C𝑖 . First, we control for splines of ambulance charges reflected in their Medicare claims. Consistent with the health economics literature on productivity and the returns to spending (Doyle et al. 2015; Chandra et al. 2016), we consider charges incurred by the ambulance company as a sufficient statistic for the intensity of treatment during the ride.38 Second, we control for splines of the mileage of the ride. Third, we control for indicators of the number of non-VA hospitals to which the ambulance company transports patients from a zip code. Fourth, we control for average measures of non-VA hospitals who which the ambulance company delivers its patients. For each non-VA hospital ℎ, we measure average mortality and spending outcomes 𝑌 ℎ , among veterans outside of our benchmark analytic sample who only have non-VA prior utilization (Panel B of Appendix Table A.13). We also measure the share, 𝑤 𝑗 ℎ , that each ambulance company 𝑗 delivers patients to each non-VA hospital ℎ, also among veterans with non-VA-only prior utilization. For each ride 𝑖, we then control for average non-VA hospital measures of mortality and Í spending, calculated as ℎ 𝑤 𝑗 (𝑖),ℎ𝑌 ℎ , weighted by the hospital-specific shares of the assigned ambulance 𝑗 (𝑖). As in Section 5.4, we use information on Medicare claims to infer non-VA hospital spending. Appendix Table A.4 shows estimates of the VA effect on mortality and on spending, using the 38 In principle, we also observe detailed CPT procedure codes for services rendered during the ambulance ride (e.g., supplemental oxygen, medications, or intravenous fluids). However, in 2002, Medicare changed to a simple payment arrangement that depended only on a few characteristics of the ride, such as ALS vs. BLS level, mileage, and the use of lights and sirens (Centers for Medicare & Medicaid Services 2002). Consistent with this payment policy, detailed CPT codes for extra services are usually missing in the claims data. A.1 same baseline controls as in our benchmark analyses in Section 3 with the addition of various ambulance related controls. We find that results are highly robust to the addition of these controls. A.1.2 Monotonicity We test the monotonicity condition in Condition 1(iii) by tests standard in the judges-design literature that demonstrate a positive first-stage relationship across subgroups of observations (Arnold et al. 2018; Bhuller et al. 2020). We define eight pairs of subsamples based on several important patient characteristics: (i) age ≤ 80 years vs. age > 80 years; (ii) white vs. non-white race; (iii) comorbidity count above vs. below median; (iv) either vs. neither mental illness or substance abuse present; (v) VA visits in the prior year above vs. below median; (vi) Advanced Life Support vs. Basic Life Support; (vii) prediction of VA user above vs. below median; and (viii) prediction of mortality above vs. below median. Under monotonicity, we expect that an ambulance that has a higher propensity to transport veterans to the VA should weakly increase the probability of transport to the VA for any set of veterans. Specifically, using the set of observations I𝑚 for each subsample 𝑚, we estimate a first-stage regression with respect to our baseline instrument, 𝑍𝑖 , from Equation (1): 𝑚 𝑚 𝐷 𝑖 = 𝜋1𝑚 𝑍𝑖 + X0𝑖 𝛿1𝑚 + 𝜁1,𝑧 (𝑖) + 𝜀 1,𝑖 , (A.1) and we assess whether 𝜋ˆ 1𝑚 ≥ 0. We further assess monotonicity in each subsample 𝑚 by constructing a “reverse-sample” instrument that only uses observations in the analytical sample (Step 6 in Appendix Table A.1) that are not in I𝑚 : 𝑍˜ 𝑖−𝑚 = 1 ∑︁ 𝐾˜ −𝑚 𝑗 (𝑖) 𝑖0 ∈ Ĩ𝑗 (𝑖) \I𝑚 1 (𝑘 (𝑖 0) ≠ 𝑘 (𝑖)) 𝐷 𝑖0 . 𝑁˜ 𝑘 (𝑖0), 𝑗 (𝑖) (A.2) Within the analytical sample, Ĩ𝑗 denotes the set of rides assigned to 𝑗, 𝐾˜ −𝑚 is the number of patients 𝑗 ˜ assigned to ambulance 𝑗 without characteristic 𝑚, and 𝑁 𝑘, 𝑗 is the number of rides by patient 𝑘 with ambulance 𝑗.39 In each subsample 𝑚, we also perform first-stage regressions of the form in Equation (A.1) that use 𝑍˜ −𝑚 instead of 𝑍𝑖 as the instrument. 𝑖 Recall that the baseline instrument, 𝑍𝑖 , is computed in the much larger sample of dually eligible veterans (Step 1 in Appendix Table A.1). Since the reverse-sample instruments are based on much smaller patient populations, they may be weaker predictors of underlying ambulance propensities to transport to the VA. In Appendix Table A.5, we demonstrate a positive and statistically significant first-stage coefficient in every subsample and for both the baseline instrument and the reverse-sample instrument. Coefficient sizes are generally smaller for the reverse-sample instruments. In Appendix Table A.6, 39 We use the analytical sample construct the reverse-sample instruments, so that the samples used to construct instruments are roughly the same between pairs of characteristics (e.g., subsamples for comorbidity count above vs. below median). A.2 we show first-stage relationships using two other instruments that are both based on the smaller analytical sample. Specifically, we construct a “baseline” instrument, 𝑍˜ 𝑖 , and an “in-sample” instrument, 𝑍˜ 𝑖𝑚 , from the analytical sample: 𝑍˜ 𝑖 = ∑︁ 1 (𝑘 (𝑖 0) ≠ 𝑘 (𝑖)) 𝐷 𝑖0 , and 𝐾˜ 𝑗 (𝑖) − 1 0 𝑁˜ 𝑘 (𝑖0), 𝑗 (𝑖) 1 (A.3) 𝑖 ∈ Ĩ𝑗 (𝑖) 𝑍˜ 𝑖𝑚 = 1 ∑︁ 𝐾˜ 𝑚 −1 𝑗 (𝑖) 𝑖0 ∈ Ĩ𝑗 (𝑖) ∩I𝑚 1 (𝑘 (𝑖 0) ≠ 𝑘 (𝑖)) 𝐷 𝑖0 . 𝑁˜ 𝑘 (𝑖0), 𝑗 (𝑖) (A.4) First-stage coefficients for these instruments are also all positive and statistically significant. They are similar in magnitude to the coefficients for the reverse-sample instruments, which suggests that lower signal-to-noise ratios due to smaller sample sizes explain much of decrease in coefficient magnitude for the reverse-sample instruments, compared to the baseline (overall-sample) instrument. A.2 Statistical Tests of Hazard Functions A.2.1 Potential Survival Rates and Hazard Rates Following the notation in Section 4, let 𝑠 𝐼 𝑉 (𝑡; 𝑑) ≡ 𝐸 [ 𝑆𝑖 (𝑡; 𝑑)| 𝑖 ∈ C] denote the IV estimands of the potential survival rates among compliers, where 𝑑 ∈ {0, 1} indicates outcomes under VA care (𝑑 = 1) or non-VA care (𝑑 = 0), for each week 𝑡 ∈ {0, 1, . . . , 52}. We then define the corresponding estimands of the potential mortality hazards as follows: ℎ 𝐼 𝑉 (𝑡; 𝑑) ≡ 𝑠 𝐼 𝑉 (𝑡 − 1; 𝑑) − 𝑠 𝐼 𝑉 (𝑡; 𝑑) . 𝑠 𝐼 𝑉 (𝑡 − 1; 𝑑) We use two-stage least squares to construct estimates of the potential survivor fractions at each time horizon, 𝑠ˆ𝐼 𝑉 (𝑡; 𝑑) and then construct the corresponding potential hazard functions, ℎˆ 𝐼 𝑉 (𝑡; 𝑑). We also construct a set of 250 block bootstrap samples (selecting samples by zip code, with replacement), and for replication sample 𝑟 ∈ {1, . . . , 𝑅}, we construct 𝑠ˆ𝑟 (𝑡; 𝑑) and ℎˆ 𝑟 (𝑡; 𝑑). Using these samples 𝐼𝑉 𝐼𝑉 we construct the mean estimated potential hazard for each week across the replications: 𝐵 ℎ 𝐼 𝑉 (𝑡; 𝑑) = 1 ∑︁ ˆ 𝑟 ℎ (𝑡; 𝑑) . 𝑅 𝑟 𝐼𝑉 (A.5) We also construct the standard deviation of the bootstrap-estimated potential hazard for each week: √︄ 𝜎 ˆ 𝐼𝐵𝑉 (𝑡; 𝑑) = i2 1 ∑︁ h ˆ 𝑟 𝐵 ℎ 𝐼 𝑉 (𝑡; 𝑑) − ℎ 𝐼 𝑉 (𝑡; 𝑑) . 𝑅−1 𝑟 (A.6) We construct similar objects for potential survival and hazard rates under OLS: 𝑠ˆ𝑂𝐿𝑆 (𝑡; 𝑑) and 𝑟 (𝑡; 𝑑) and ℎˆ 𝑂𝐿𝑆 (𝑡; 𝑑), respectively. Using the same set of block bootstrap samples, we compute 𝑠ˆ𝑂𝐿𝑆 (𝑡; 𝑑) in each bootstrap replication sample 𝑟. ℎˆ 𝑟 𝑂𝐿𝑆 A.3 A.2.2 Test of Mortality Displacement To detect “mortality displacement” (Schwartz 2000), in which deaths of VA patients are simply delayed, we test the joint null hypothesis that ℎ 𝐼 𝑉 (𝑡; 1) ≤ ℎ 𝐼 𝑉 (𝑡; 0) for all 𝑡 ≥ 1. This null hypothesis states that the mortality hazard under the VA never overtakes the mortality hazard under non-VA hospitals, even in later periods, and it is consistent with no mortality displacement. Restating the null hypothesis as 𝐻0,1 : ℎ 𝐼 𝑉 (𝑡; 0) − ℎ 𝐼 𝑉 (𝑡; 1) ≥ 0, for all 𝑡 ≥ 1, (A.7) we use estimates ℎˆ 𝐼 𝑉 (𝑡; 0) − ℎˆ 𝐼 𝑉 (𝑡; 1) and consider the following test statistic of the null, based on Wolak (1987): 𝑄1 ≡ 52 ∑︁   2 𝑤 1,𝑡 1 ℎˆ 𝐼 𝑉 (𝑡; 0) − ℎˆ 𝐼 𝑉 (𝑡; 1) < 0 ℎˆ 𝐼 𝑉 (𝑡; 0) − ℎˆ 𝐼 𝑉 (𝑡; 1) (𝑡) , (A.8) 𝑡=1 where 𝑤 1,𝑡 is a strictly positive weight. This test statistic penalizes only negative differences ℎˆ 𝐼 𝑉 (𝑡; 0) − ℎˆ 𝐼 𝑉 (𝑡; 1) < 0 that can be consistent with the null hypothesis that ℎˆ 𝐼 𝑉 (𝑡; 0) − ℎˆ 𝐼 𝑉 (𝑡; 1) ≥ 0, for all 𝑡 ≥ 1, only by statistical noise. To derive a critical value for 𝑄 1 , we use our bootstrap sample to form a set of recentered bootstrap estimates of the potential hazards at each week: 𝐵 ℎ˜ 𝑟𝐼 𝑉 (𝑡; 0) = ℎˆ 𝑟𝐼 𝑉 (𝑡; 0) − ℎ 𝐼 𝑉 (𝑡; 0) ; 𝐵 ℎ˜ 𝑟𝐼 𝑉 (𝑡; 1) = ℎˆ 𝑟𝐼 𝑉 (𝑡; 1) − ℎ 𝐼 𝑉 (𝑡; 1) . We then construct the empirical distribution of the test statistic, in Equation (A.8), under the recentered bootstrap deviations: 𝑄 𝑟1 ≡ 52 ∑︁

2 𝑤 1,𝑡 1 ℎ˜ 𝑟𝐼 𝑉 (𝑡; 0) − ℎ˜ 𝑟𝐼 𝑉 (𝑡; 1) < 0 ℎ˜ 𝑟𝐼 𝑉 (𝑡; 0) − ℎ˜ 𝑟𝐼 𝑉 (𝑡; 1) . (A.9) 𝑡=1 We take the 95th percentile of this distribution as the critical value above which our test statistic 𝑄 1 can reject the null hypothesis 𝐻0,1 , in Equation (A.7). Following Wolak (1987), this distribution is formed under the data generating process implied by the “least favorable null” for testing joint inequality constraints (Perlman 1969). Specifically, we consider the least favorable data generating process that satisfies the null hypothesis 𝐻0 , in Equation (A.7), which is 𝐻 0,1 : ℎ 𝐼 𝑉 (𝑡; 0) − ℎ 𝐼 𝑉 (𝑡; 1) = 0, for all 𝑡 ≥ 1. (A.10) If we obtain a test statistic 𝑄 1 with improbable negative deviations that reject the least favorable null hypothesis 𝐻 0,1 in Equation (A.10), then we can also reject the null hypothesis 𝐻0,1 in Equation (A.7). A.4 We use the same weights 𝑤 1,𝑡 in Equations (A.8) and (A.9) and set them as the inverse of the estimated sampling variance of the recentered deviations: 𝑤 −1 1,𝑡 =
2 1 ∑︁ ˜ 𝑟 ℎ 𝐼 𝑉 (𝑡; 0) − ℎ˜ 𝑟𝐼 𝑉 (𝑡; 1) . 𝑅−1 𝑟 (A.11) These weights standardize the statistical distribution of ℎˆ 𝐼 𝑉 (𝑡; 0) − ℎˆ 𝐼 𝑉 (𝑡; 1), so that the test statistic distribution can be considered as chi-squared. Although we use critical values derived from the bootstrap distribution, we find the scale of our test statistic to be more intuitive with this normalization.40 We show results in Panel A of Appendix Figure A.4. We find that 𝑄 1 is within the distribution of bootstrapped values of 𝑄 𝑟1 . We therefore cannot reject the null of no mortality displacement. A.2.3 Extended Test of IV Validity In addition to standard tests of IV validity that are based on observable characteristics—including tests of balance in Section 3.2 and monotonicity in Appendix A.1.2—we develop a tractable extended test of IV validity using the insights in Balke and Pearl (1997) and Heckman and Vytlacil (2005, Proposition A.5) that are based on potential outcomes. Kitagawa (2015) summarizes these insights as follows for a binary instrument 𝑍 ∈ {0, 1}, a binary treatment 𝐷 ∈ {0, 1} (increasing in probability with 𝑍), and an outcome 𝑌 ∈ Y. For any Borel set 𝐵 in Y, IV validity in Condition 1 implies that Pr (𝑌 ∈ 𝐵, 𝐷 = 1| 𝑍 = 1) − Pr (𝑌 ∈ 𝐵, 𝐷 = 1| 𝑍 = 0) ≥ 0; (A.12) Pr (𝑌 ∈ 𝐵, 𝐷 = 0| 𝑍 = 0) − Pr (𝑌 ∈ 𝐵, 𝐷 = 0| 𝑍 = 1) ≥ 0. (A.13) Kitagawa (2015, Proposition 1.1) further states that tests of Equations (A.12) and (A.13) constitute the strongest possible tests of IV validity in the sense that no other feature of the data can contribute further to screening out invalid instruments.41 We note that, given the approach in Abadie (2002), testing Equations (A.12) and (A.13) is algebraically equivalent to testing, for all 𝐵 ⊂ Y, Pr (𝑌𝑖 (0) ∈ 𝐵| 𝑖 ∈ C) ≥ 0; (A.14) Pr (𝑌𝑖 (1) ∈ 𝐵| 𝑖 ∈ C) ≥ 0. (A.15) 40 Wolak (1987) proposes to use an optimal minimum distance test statistic that would use the full covariance matrix of 𝛿 (𝑡). We avoid this formulation due to finite-sample issues that would cause this covariance matrix to be poorly estimated by the full covariance matrix of 𝛿˜𝑟 (𝑡), noted by Altonji and Segal (1996). Results are qualitatively similar when we choose a weight of 𝑤 𝑡 = 1 for all 𝑡, but we find that using 𝑤 𝑡 from Equation (A.11)—i.e., normalizing each 𝛿 (𝑡) by its bootstrap standard error—affords greater power in rejecting the null. This approach is equivalent to our best estimate of a diagonal covariance matrix in place of the full covariance matrix. 41 Chan et al. (2019) provides an applied example, in the setting of radiologists, in which standard monotonicity tests in Appendix A.1.2 are satisfied but a simple version of this extended test of validity is not satisfied. They find that radiologists who diagnose more cases with pneumonia do so in a wide range of subgroups of patients defined by observable characteristics (i.e., standard tests of monotonicity) but that the same radiologists who diagnose more cases with pneumonia are more likely to miss cases of pneumonia (i.e., Pr (|𝑌 ∈ 𝐵, 𝐷 = 0 𝑍 = 0) − Pr (|𝑌 ∈ 𝐵, 𝐷 = 0 𝑍 = 1) < 0). A.5 Thus we use the Abadie (2002) approach to define a partition of mortality outcomes Y in terms of weekly hazard rates, by the date of death (if any) following the ambulance ride. Such a partition implies that potential hazard rates among compliers, ℎ 𝐼 𝑉 (𝑡; 𝑑), are non-negative in every week 𝑡 ∈ {1, . . . , 52} under both VA assignment (𝑑 = 1) and non-VA assignment (𝑑 = 0). That is, our extended test of IV validity amounts to testing the following joint null hypothesis of inequality constraints: 𝐻0,2 : ℎ 𝐼 𝑉 (𝑡; 𝑑) ≥ 0, for all 𝑡 ≥ 1, 𝑑 ∈ {0, 1} . (A.16) Following a similar approach as for mortality displacement in Appendix A.2.2, our test statistic is 𝑄2 ≡ 1 ∑︁ 52 ∑︁   2 𝑤 2,𝑡 1 ℎˆ 𝐼 𝑉 (𝑡; 𝑑) < 0 ℎˆ 𝐼 𝑉 (𝑡; 𝑑) , 𝑑=0 𝑡=1
2 ˆ 𝐼𝐵𝑉 (𝑡; 𝑑) . We obtain the critical value for our test statistic by the distribution of where 𝑤 −1 2,𝑡 = 𝜎 recentered bootstrapped estimates, defined above. For the 𝑟th bootstrap replication, the test statistic is 𝑄 𝑟2 ≡ 1 ∑︁ 52 ∑︁

2 𝑤 2,𝑡 1 ℎ˜ 𝑟𝐼 𝑉 (𝑡; 𝑑) < 0 ℎ˜ 𝑟𝐼 𝑉 (𝑡; 𝑑) . 𝑑=0 𝑡=1 We take the 95th percentile of the distribution of 𝑄 𝑟2 across replications 𝑟 ∈ {1, . . . , 𝑅} as the critical value for 𝑄 2 . As above, this test of inequality constraints is based upon a least favorable null hypothesis. In this case, the least favorable null hypothesis is 𝐻 0,2 : ℎ 𝐼 𝑉 (𝑡; 𝑑) = 0, for all 𝑡 ≥ 1, 𝑑 ∈ {0, 1} . (A.17) We show results in Panel B of Appendix Figure A.4. We find that 𝑄 2 is lower than any bootstrapped value of 𝑄 𝑟2 . This suggests not only that we cannot reject the null hypothesis 𝐻0,2 in Equation (A.16), but also that the realized data are significantly more favorable than the least favorable null hypothesis 𝐻 0,2 in Equation (A.17). In other words we can strongly reject the null that ℎ 𝐼 𝑉 (𝑡; 𝑑) = 0, for all 𝑡 ≥ 1, 𝑑 ∈ {0, 1}, which means that ℎ 𝐼 𝑉 (𝑡; 𝑑) > 0 for at least some 𝑡 ≥ 1, 𝑑 ∈ {0, 1}. A.2.4 Tests of Hazard Rate Equality We finally perform tests of the equality of hazard rates after the first week after the ambulance ride. Comparing hazard rates across different groups of veterans, we aim to shed light on heterogeneity in longer-term mortality risk across these groups. To define these tests generally, consider two sets of hazard rates, ℎ1 (𝑡) and ℎ2 (𝑡), for 𝑡 ≥ 2. We consider two types of null hypothesis. First, we assess mean differences in hazard rates between {ℎ1 (𝑡)}𝑡 and {ℎ2 (𝑡)}𝑡 , for 𝑡 ≥ 1, under the null hypothesis that the mean hazard rate is the same between the two sets: 52 1 ∑︁ (ℎ1 (𝑡) − ℎ2 (𝑡)) = 0. 𝐻0,3 : 51 𝑡=2 A.6 (A.18) We test this null hypothesis by comparing  Í52  ˆ ˆ 2 (𝑡) against the bootstrapped distri(𝑡) − ℎ ℎ 1 𝑡=2 1 51 bution of recentered differences. Specifically, for replication 𝑟 ∈ {1, . . . , 𝑅}, denote the bootstrap  𝑟 𝑟 ˆ ˆ estimate hazard rates of (ℎ1 (𝑡) , ℎ2 (𝑡)) as ℎ (𝑡) , ℎ (𝑡) . Define the recentered bootstrap hazard rate 1 2 as 𝐵 ℎ˜ 𝑟1 (𝑡) ≡ ℎˆ 𝑟1 (𝑡) − ℎ1 (𝑡) and 𝐵 ℎ˜ 𝑟2 (𝑡) ≡ ℎˆ 𝑟2 (𝑡) − ℎ2 (𝑡) , 𝐵 where ℎ1 (𝑡) ≡ 1 𝑅 Í 𝑟 𝐵 ℎ1 (𝑡) and ℎ2 (𝑡) ≡ 1 𝑅 Í 𝑟 ℎ2 (𝑡). The distribution of  1 51 Í52 𝑡=2 ℎ˜ 𝑟1 (𝑡) − ℎ˜ 𝑟2 (𝑡)
𝑟 determines the two-sided critical values for the mean hazard difference. By construction, this distribution will have mean 0. Second, we consider the joint null hypothesis that the difference between each pair of hazards is equal to 0: 𝐻0,4 : ℎ1 (𝑡) − ℎ2 (𝑡) = 0, for all 𝑡 ≥ 1. (A.19) Using estimates ℎˆ 1 (𝑡) − ℎˆ 2 (𝑡), we construct the following test statistic: 𝑄 4 (ℎ1 (·) , ℎ2 (·)) ≡ 52 ∑︁  2 𝑤 4,𝑡 ℎˆ 1 (𝑡) − ℎˆ 2 (𝑡) . 𝑡=2 We compute the empirical distribution of 𝑄 4 under the null hypothesis by using recentered differences ℎ˜ 𝑟 (𝑡) − ℎ˜ 𝑟 (𝑡). Each bootstrap replication 𝑟 yields 1 2 𝑄 𝑟4 (ℎ1 (·) , ℎ2 (·)) ≡ 52 ∑︁
2 𝑤 4,𝑡 ℎ˜ 𝑟1 (𝑡) − ℎ˜ 𝑟2 (𝑡) . 𝑡=2 We take the 95th percentile of the distribution of 𝑄 𝑟4 across replications 𝑟 ∈ {1, . . . , 𝑅} as the critical  2 1 Í e𝑟 𝑟 (𝑡) e (𝑡) ℎ − ℎ to standardize the distribution of ℎˆ 1 (𝑡) − ℎˆ 2 (𝑡). value for 𝑄 4 . We set 𝑤 −1 = 𝑅−1 𝑟 1 2 4,𝑡 In Appendix Figures A.5 and A.6, we consider five comparisons of hazard rates, for 𝑡 ≥ 1, under the null hypotheses of Equations (A.18) and (A.19), respectively. First, we test the null hypothesis that ℎ 𝐼 𝑉 (𝑡; 1) − ℎ 𝐼 𝑉 (𝑡; 0) = 0, for all 𝑡 ≥ 1. Under quasi-experimental assignment of compliers (Condition 1), we expect not to reject this null if longer-term hazard rates reflect underlying health. Second, we test the null hypothesis that ℎ𝑂𝐿𝑆 (𝑡; 1) − ℎ𝑂𝐿𝑆 (𝑡; 0) = 0, for all 𝑡 ≥ 1. While we show stability of OLS results in Figure 2, this test may reveal differences in underlying health between veterans assigned to the VA and those assigned to a non-VA hospital that are not captured by observable patient characteristics. Third, we test the null hypothesis that ℎ 𝐼 𝑉 (𝑡; 1) − ℎ𝑂𝐿𝑆 (𝑡; 1) = 0, for all 𝑡 ≥ 1. This reveals differences in underlying health between compliers and VA-assigned veterans, which includes compliers and always takers. Fourth, we similarly test the null hypothesis that ℎ 𝐼 𝑉 (𝑡; 0) − ℎ𝑂𝐿𝑆 (𝑡; 0) = 0, for all 𝑡 ≥ 1. This reveals differences in underlying health between compliers and non-VA-assigned veterans, which includes compliers and never takers. A.7 A.3 Non-Complier Characteristics In this appendix section, we describe a simple approach to calculate characteristics of non-compliers, following Dahl et al. (2014), and we discuss results. In our approach, we first residualize the leave-out
ambulance propensity to transport to the VA, 𝑍𝑖 , by our key controls, 𝑧 (𝑖) , X0𝑖 . Denote this residual as 𝑍𝑖∗ . We categorize always takers as rides with 𝑍𝑖∗ below the 20th percentile that still went to the VA (𝐷 𝑖 = 1). We categorize never takers as rides with 𝑍𝑖∗ above the 80th percentile that still did not go to the VA (𝐷 𝑖 = 0). Among each group of always takers and never takers, we compute characteristics along the same dimensions as those in our compliers analysis, in Table 4. Specifically, for each characteristic, we compute mean values among the group of always takers and among the group of never takers, and we compare these means with the overall mean by a ratio. We compute standard errors of these means by drawing bootstrapped samples, blocked by zip code, and repeating this procedure with each bootstrapped sample. As shown in Appendix Table A.7, we mostly find results that are consistent with our earlier results of complier characteristics and the fact that the majority of non-compliers are never takers: For many characteristics, those that are more common among compliers tend to be more common among always takers and less common among never takers. Compared to the overall population, always takers are more likely to be Black and have lower income. Always takers are more likely to have mental illness, and they have a slightly higher rate of substance abuse, though the latter is not statistically significant. Always takers are more likely to have prior VA ED visits and less likely to have prior non-VA ED visits. However, both always takers and never takers as defined by this methodology have slightly higher predicted mortality. A.4 Marginal and Average Treatment Effects Consider the probability of going to the VA as a function of our instrument 𝑍𝑖 and key controls
𝑧 (𝑖) , X0𝑖 : 𝑃 (𝑍𝑖 ), where we have omitted the key controls for brevity. Following Heckman and Vytlacil (2005), we can state the treatment rule as 𝐷 𝑖 = 1 (𝑃 (𝑍𝑖 ) ≥ 𝑈𝑖 ) , (A.20) where 𝑈𝑖 is uniformly distributed in the interval (0, 1). Individuals with low 𝑈𝑖 relative to 𝑝 ≡ arg min𝑖 𝑃 (𝑍𝑖 ) are always takers, while individuals with high 𝑈𝑖 relative to 𝑝 ≡ arg max𝑖 𝑃 (𝑍𝑖 ) are never takers. In this appendix, we estimate two objects relative to selection, as defined by 𝑈𝑖 ∼ 𝑈 (0, 1). The marginal treatment effect (MTE) for rides with 𝑈𝑖 = 𝑢 is 𝑀𝑇 𝐸 (𝑢) ≡ 𝐸 [𝑌𝑖 (1) −𝑌𝑖 (0)| 𝑈𝑖 = 𝑢] . A.8 The average treatment effect (ATE) is 1 ∫ 𝑀𝑇 𝐸 (𝑢) 𝑑𝑢. 𝐴𝑇 𝐸 = 0 i h We estimate 𝑀𝑇 𝐸 (𝑢), for 𝑢 ∈ 𝑝, 𝑝 , using variation in the propensity of ambulances to transport to the VA. We estimate the ATE by extrapolating 𝑀𝑇 𝐸 (𝑢) to 𝑢 ∈ [0, 1] with a control function approach. A.4.1 Marginal Treatment Effects We first estimate marginal treatment effects using a local instrumental variables approach that exploits outcomes along the distribution of ambulance propensity to transport to the VA. The intuition for this approach is that 𝑀𝑇 𝐸 (𝑢) can be stated as 𝑀𝑇 𝐸 (𝑢) = 𝜕 𝐸 [𝑌𝑖 | 𝑃 (𝑍𝑖 ) = 𝑢] . 𝜕𝑝 That is, if mortality decreases linearly with ambulance propensity to transport to the VA, then the data would be consistent with constant treatment effects. On the other hand, if mortality decreases at a faster rate for lower 𝑃 (𝑍𝑖 ), then the data would suggest “selection on gains,” in which veterans who are more likely to benefit from VA care are also more likely to be transported to the VA given a set of ambulances. The visual IV relationship in Appendix Figure A.1 suggests a slightly convex shape in the relationship between mortality and 𝑃 (𝑍𝑖 ), which implies selection on gains. We proceed with estimating a flexible relationship between 𝑌𝑖 and 𝑃 (𝑍𝑖 ) as follows. We compute 𝑃 (𝑍𝑖 ) = 𝐷ˆ 𝑖 from the first-stage Equation (3). We then residualize 𝐷ˆ 𝑖 by baseline controls, defined in Appendix Table A.2, and denote the residual as 𝐷ˆ ∗𝑖 . We similarly residualize 𝑌𝑖 by baseline controls and denote the residual as 𝑌 ∗ . For interpretation, we set 𝑌 ∗ and 𝐷ˆ ∗ to have the same respective means 𝑖 𝑖 𝑖 as 𝑌𝑖 and 𝐷 𝑖 . A regression of 𝑌𝑖∗ on 𝐷ˆ ∗𝑖 yields a point estimate that is numerically identical to the IV estimate 𝛽ˆ𝐼 𝑉 .42
Rather than fitting a straight line through points 𝐷ˆ ∗𝑖 ,𝑌𝑖∗ , we fit a flexible function with Gaussian basis splines with four knots (𝑘 1 , 𝑘 2 , 𝑘 3 , 𝑘 4 ) corresponding to the 5th, 35th, 65th, and 95th percentiles of 𝐷ˆ ∗ . Specifically, for each ride 𝑖, we form five basis functions 𝑖   𝑓𝑛 ( 𝑝) = exp − (𝑘 𝑛 − 𝑘 𝑛−1 ) ( 𝑝 − 𝑐 𝑛 ) 2 , where 𝑐 𝑛 = 12 (𝑘 𝑛−1 + 𝑘 𝑛 ), 𝑘 0 = min 𝐷ˆ ∗𝑖 , and 𝑘 5 = max 𝐷ˆ ∗𝑖 . We regress 𝑌𝑖∗ = 5 ∑︁
𝛾𝑛 𝑓𝑛 𝐷ˆ ∗𝑖 + 𝜀𝑖 𝑛=1 Í and form a flexible prediction 𝑌ˆ ∗ ( 𝑝) = 5𝑛=1 𝛾ˆ 𝑛 𝑓𝑛 ( 𝑝). 42 This regression corresponds to the indirect least squares version of IV and is also numerically identical to the visual IV coefficient that corresponds to the two-stage least squares version of IV. A.9 This prediction yields a convenient analytical derivative for the MTE š𝐸 (𝑢) = 𝑀𝑇 5 ∑︁ 𝛾ˆ 𝑛 𝑓𝑛0 (𝑢) = − 𝑛=1 5 ∑︁ 2 (𝑘 𝑛 − 𝑘 𝑛−1 ) 2 (𝑢 − 𝑐 𝑛 ) 𝛾ˆ 𝑛 𝑓𝑛 (𝑢) . 𝑛=1 For each 𝑝 ∈ [0.05, 0.20], corresponding to the range of 𝐷ˆ ∗𝑖 , we compute 95% confidence intervals of 𝑌ˆ ∗ ( 𝑝) by taking the standard deviations of 𝑌ˆ ∗ ( 𝑝) across 50 bootstrapped iterations (with samples drawn by zip code, with replacement). Similarly, for each 𝑢 ∈ [0.05, 0.20], we compute 95% š𝐸 (𝑢) by taking the standard deviations of 𝑀𝑇 š𝐸 (𝑢) across these same confidence intervals of 𝑀𝑇 š𝐸 (𝑢) in Appendix Figure A.7. bootstrapped iterations. We display both 𝑌ˆ ∗ ( 𝑝) and 𝑀𝑇 A.4.2 Average Treatment Effect In order to estimate the ATE, we adopt a control function model in order to extrapolate treatment effects to non-compliers. Specifically, we model potential outcomes as 𝐸 [𝑌𝑖 (𝑑)| 𝑈𝑖 = 𝑢] = 𝛼𝑑 + 𝛾 𝑑 (𝐽 (𝑢) − 𝜇 𝐽 ) + X0𝑖 𝛿 + 𝜁 𝑧 (𝑖) , (A.21) where 𝑑 ∈ {0, 1} and 𝑢 ∈ (0, 1). 𝐽 (𝑢) is a strictly increasing, continuous function that maps selection to potential outcomes, and 𝜇 𝐽 ≡ 𝐸 [𝐽 (𝑈𝑖 )]. Since 𝐸 [𝐽 (𝑢) − 𝜇 𝐽 ] = 0, we can interpret 𝛼1 − 𝛼0 as the ATE. Kline and Walters (2019) show that the control function model in Equations (A.20) and (A.21) can also rationalize the Imbens and Angrist (1994) LATE that we estimate in Section 3, regardless of the choice of 𝐽 (𝑢).43 For our baseline specification, we adopt the linear selection function of 𝐽 (𝑢) = 𝑢 from Olsen (1980), which we use with Equation (A.21) to state the following expectation, conditional on the first-stage error 𝜀 1,𝑖 from Equation (3):44   𝐸 𝑌𝑖 | 𝐷 𝑖 = 𝑑, 𝜀 1,𝑖 = 𝜀   = 𝛼𝑑 + 𝛾 𝑑 𝐸 𝐽 (𝑢) − 𝜇 𝐽 | 𝐷 𝑖 = 𝑑, 𝜀 1,𝑖 = 𝜀 + X0𝑖 𝛿 + 𝜁 𝑧 (𝑖) 𝜀 = 𝛼𝑑 − 𝛾 𝑑 + X∗𝑖 𝛿 + 𝜁 𝑧 (𝑖) . 2 (A.22) This expectation corresponds to the following regression:  𝑌𝑖 = 𝛼Δ 𝐷 𝑖 + 𝛾0    𝜀ˆ1,𝑖 𝜀ˆ1,𝑖 − + 𝛾Δ − 𝐷 𝑖 + X0𝑖 𝛿 + 𝜁 𝑧 (𝑖) + 𝑣 𝑖 , 2 2 (A.23) plugging in the estimated first-stage residual 𝜀ˆ1,𝑖 from Equation (3). We can compute the ATE from 43 Kline and Walters (2019) show algebraic equivalence between the control function LATE implied by Equation (A.21), 𝑝, and 𝑝, when the instrument is binary and there are no controls. They also generalize their result for multivalued instruments. With controls, the equivalence may not hold in the standard regression approach in which controls are treated as additively separable but will hold under a propensity score approach. 44 To see this, assume that the first stage regression in Equation (3) estimates a well-behaved 𝑃 (𝑍 ) ∈ (0, 1) such that 𝑖 𝑝 𝑝−1 𝐷 𝑖 = 𝑃 (𝑍𝑖 ) + 𝜀 1,𝑖 . Define 𝜆 𝑑 ( 𝑝) ≡ 𝐸 [ 𝐽 (𝑈𝑖 ) − 𝜇 𝐽 | 𝐷 𝑖 = 𝑑, 𝑃 (𝑍𝑖 ) = 𝑝]. We have 𝜆 1 ( 𝑝) = 2 − 12 = 2 , and 𝜆0 ( 𝑝) = − 12 = 2 . Note that 𝜆 𝑑 ( 𝑝) = 2 = −𝜀 statistic 2 , where 𝜀 ≡ 𝑑 − 𝑝. This implies that 𝜀 1,𝑖 = 𝐷 𝑖 − 𝑃 (𝑍 𝑖 ) is a sufficient  for (𝐷 𝑖 , 𝑃 (𝑍𝑖 )), and we can state the expectation 𝐽 (𝑈𝑖 ) − 𝜇 𝐽 conditional on 𝜀 1,𝑖 : 𝐸 𝐽 (𝑈𝑖 ) − 𝜇 𝐽 | 𝜀 1,𝑖 = 𝜀 = − 2𝜀 . 𝑝+1 2 𝑝 𝑝−𝑑 A.10 this equation as 𝛼Δ = 𝛼1 − 𝛼0 . We estimate Equation (A.23) by OLS to yield 𝛼ˆ Δ = −0.037 , slightly smaller in magnitude than the LATE estimate of −0.041 from Section 3. For inference on the difference between the ATE and the LATE, we recover a numerically equivalent LATE with the following control function regression:45 𝑌𝑖 = 𝛽𝐶𝐹 𝐷 𝑖 + 𝛾 𝜀ˆ1,𝑖 + X0𝑖 𝛿0 + 𝜁0,𝑧 (𝑖) + 𝑣 𝑖 , (A.24) where 𝛽ˆ𝐶𝐹 is estimated by OLS and is numerically equivalent to 𝛽ˆ𝐼 𝑉 estimated by two-stage least squares. For each bootstrapped replication, we estimate both the ATE, 𝛼ˆ 1 − 𝛼ˆ 0 , and its difference with the LATE, 𝛽ˆ𝐶𝐹 , in order to obtain standard errors on both the ATE and the difference. We also examine semiparametric specifications that allow for flexible relationships between the first-stage residual and the structural error term. These alternative specifications allow nonlinear   relationships of 𝑔 𝑑 (𝜀) ≡ 𝐸 𝜀0,𝑖 𝐷 𝑖 = 𝑑, 𝜀 1,𝑖 = 𝜀 , where 𝜀0,𝑖 is the structural error term in Equation (2). Specifically, we estimate regressions of the following form:

𝑌𝑖 = 𝛼Δ 𝐷 𝑖 + 𝑔0 𝜀ˆ1,𝑖 (1 − 𝐷 𝑖 ) + 𝑔1 𝜀ˆ1,𝑖 𝐷 𝑖 + X0𝑖 𝛿 + 𝜁 𝑧 (𝑖) + 𝑣 𝑖 , (A.25)
where 𝑔 𝑑 𝜀ˆ1,𝑖 , 𝑑 ∈ {0, 1}, are flexible functions of the first-stage residual that are non-zero when
𝐷 𝑖 = 0 and 𝐷 𝑖 = 1, respectively. To estimate 𝑔 𝑑 𝜀ˆ1,𝑖 , 𝑑 ∈ {0, 1}, we use a vector of restricted cubic 
 spline functions or Gaussian basis functions, with three or five knots. Ensuring that 𝐸 𝑔 𝑑 𝜀ˆ1,𝑖 = 0 by demeaning each spline or basis function, we can interpret 𝛼Δ as the ATE. In Appendix Table A.8, we show estimates of the ATE and the ATE-LATE difference. ATE estimates are all smaller in magnitude than the LATE estimate from Section 3. We compute standard errors on this difference with 50 bootstrapped iterations (selecting samples by zip code, with replacement). The ATE-LATE difference is statistically significant in our baseline specification in Equation (A.23), though they are not statistically significant in the semiparametric specifications. A.5 Hospital Characteristics In this appendix, we provide further details on hospital characteristics that we use in our heterogeneity analyses in Section 5.3. For each zip code and year, we use characteristics of the closest VA hospital and a weighted average of the characteristics of associated non-VA hospitals. Weights for each nonVA hospital are proportional to the number of ambulance rides originating from a given zip code to the hospital in that year. Unless otherwise noted, characteristics are observed at the hospital-year level. We use the American Hospital Association (AHA) Annual Survey to collect the following VA and non-VA hospital characteristics at the hospital-year level: (i) number of ED visits; (ii) number of facility admissions; (iii) number of available hospital beds; (iv) teaching hospital status; (v) trauma 45 Blundell and Matzkin (2014) attribute the first proof of this equivalence between control function and two-stage least squares approaches to estimating the LATE to Telser (1964). A.11 center status; (vi) number of privileged ED staff, which we use to construct ED staff per 100 ED visits given (i); (vii) number of full-time registered nurses, which we use to construct nurses per 100 admissions given (ii); (viii) number of privileged hospitalists, which we use to construct hospitalists per 100 admissions; and (ix) number of privileged intensivists, which we use to construct intensivists per 100 admissions given (ii). We construct a measure of advanced cardiac care, which we define as either the capability to perform interventional cardiac catheterization or cardiac surgery as measured by the AHA Annual Survey (at the hospital-year level) or listing as an ST-Elevation Myocardial Infarction (STEMI) center by the American Heart Association (at the hospital level). We record whether each hospital is certified as a Primary Stroke Center according to the Joint Commission, the American Heart Association, and the American Stroke Association (at the hospital level). For VA hospitals, we form measures of relative spending from the average cost of an inpatientday, available from the VA Health Economics Resource Center (HERC). For non-VA hospitals, we use data from Data.Medicare.gov on Medicare spending per beneficiary at the hospital level. Similarly, we obtain mortality and readmission rates from Data.Medicare.gov for non-VA hospitals and from the VA’s Strategic Analytics for Improvement and Learning (SAIL). For each hospital’s mortality rate, we take the mean of all available 30-day mortality rates, including disease-specific rates such as heart attack and pneumonia; we form similar means for each hospital’s readmission rate based on available 30-day readmission rates, including disease-specific rates. Because some years are missing mortality or readmission rates, for each hospital and rate, we first form averages across years at the hospital level. For measures of non-VA hospital organization, we use AHA Annual Survey measures of network status, hospital system status, and health maintenance organization (HMO) affiliation. We also obtain whether the hospital participates in an Affordable Care Organization (ACO) from the Medicare Shared Savings Program (MSSP) ACO provider-level dataset. We measure health IT adoption for each hospital and year from electronic health record certified products measured in healthIT.gov. Additional characteristics in Table 5 are also obtained from the AHA Annual Survey: (i) average daily census, (ii) urban location (i.e., hospital is not classified as either “micro” or rural), (iii) capitated lives covered, and (iv) Preferred Provider Organization (PPO) affiliation. A.6 OLS Heterogeneity in Station-Specific VA Advantage In this appendix, we describe analyses related to OLS heterogeneity in the station-specific VA advantage and validating this heterogeneity with our quasi-experiment. As in our heterogeneity analyses in Section 5.3, we assign each zip code 𝑧 to a VA station ℓ (𝑧) based on the station that the most veterans living in that zip code use. This assignment of zip codes to VA stations matches station catchment areas for 92% of zip codes. A.12 In separate OLS regressions, we estimate the VA advantage for each station ℓ as 𝛽ℓ in ℓ 𝑌𝑖 = 𝛽𝑂𝐿𝑆 𝐷 𝑖 + X0𝑖 𝛿ℓ + 𝜁 𝑧ℓ (𝑖) + 𝜀 𝑖 , (A.26) using ambulance rides 𝑖 such that the zip code 𝑧 (𝑖) maps to station ℓ (i.e., ℓ (𝑖) ≡ ℓ (𝑧 (𝑖)) = ℓ). The ride-weighted variance of 𝛽ˆℓ is 3.4 × 10−4 , while the ride-weighted variance of the sampling error 𝑂𝐿𝑆 ℓ ℓ for each 𝛽ˆ𝑂𝐿𝑆 is 2.1 × 10−4 . This implies a sampling-error-adjusted, ride-weighted variance of 𝛽𝑂𝐿𝑆 √ ℓ of 𝐴 = (3.4 − 2.1) × 10−4 = 1.4 × 10−4 , or a standard deviation of 𝛽𝑂𝐿𝑆 of 𝐴 = 0.012. In Appendix Figure A.8, we plot the distribution of 𝛽ˆℓ for 32 stations with at least 5,000 rides, 𝑂𝐿𝑆 forming a smple of 276, 483 rides. We also plot the empirical Bayes posteriors for all stations, which we calculate as follows: ℓ ℓ 𝛽˜𝑂𝐿𝑆 = (1 − 𝐵ℓ ) 𝛽ˆ𝑂𝐿𝑆 + 𝐵ℓ 𝛽ˆ𝑂𝐿𝑆 , where 𝐵ℓ = (A.27) 𝑉ℓ 𝑉ℓ +𝐴 is the shrinkage factor based on 𝑉ℓ , which is the variance of the sampling error for ℓ station ℓ, and 𝐴, which is the variance of the prior distribution of 𝛽𝑂𝐿𝑆 . 𝛽ˆ𝑂𝐿𝑆 = −0.024 is the overall OLS estimate reported in Section 3.3. This figure shows that essentially all stations exhibit a VA advantage, at least when estimated by OLS. ℓ We evaluate whether differences in 𝛽˜𝑂𝐿𝑆 imply differences in the treatment effects identified by our quasi-experiment. As a first analysis, we divide stations into two groups depending on whether 𝛽˜ℓ is above- or below-median. We estimate by two-stage least squares 𝛽ˆ𝐼 𝑉 , based on Equations 𝑂𝐿𝑆 (3) and (4), separate IV estimates for ambulance rides belonging to each of these two groups. 𝛽ˆ𝐼 𝑉 estimated for stations with below-median (i.e., larger in magnitude) 𝛽˜ℓ is 0.030 larger in magnitude 𝑂𝐿𝑆 ℓ than the same estimate for stations with above-median (i.e., smaller in magnitude) 𝛽˜𝑂𝐿𝑆 . However, the difference is imprecise, with a bootstrapped standard error of 0.051. ℓ For a more systematic validation of 𝛽˜𝑂𝐿𝑆 , in the spirit of Angrist et al. (2017), we conduct a ℓ ℓ∗ , we estimate pooled analysis by indirect least squares. Specifically, denoting demeaned 𝛽˜𝑂𝐿𝑆 as 𝛽˜𝑂𝐿𝑆 ℓ (𝑖)∗ + X0𝑖 𝛿 + 𝜁 𝑧 (𝑖) + 𝜀 𝑖 , 𝑌𝑖 = 𝛽𝐷 𝑖 + 𝛾𝐷 𝑖 × 𝛽˜𝑂𝐿𝑆 ℓ (𝑖)∗ ℓ (𝑖)∗ by 𝑍𝑖 and 𝑍𝑖 × 𝛽˜𝑂𝐿𝑆 . This regression reveals an imprecise and where we instrument 𝐷 𝑖 and 𝐷 𝑖 × 𝛽˜𝑂𝐿𝑆 wrong-signed result of 𝛾ˆ = −0.790 (s.e., 1.351). The overall imprecision of these results suggests that there is little signal that we can validate in the heterogeneity across station-specific OLS measures of the VA advantage. The more precise results in Section 5.3 also suggest little meaningful heterogeneity along binary characteristics of VA and non-VA hospitals in a given zip code. A.7 Modal-Hospital Mechanisms In Section 5.5, we investigate the role of health IT and integrated care in improving outcomes for patients with prior care at a given non-VA hospital. As described in Appendix A.5, we measures dates of hospital health IT adoption or ACO participation. During our sample period a sizable proportion of hospitals adopted health IT and, to a much lesser extent, participated in an ACO. In Figure 6, we A.13 show that the survival effect of a veteran being transported to his modal hospital emerges after the passage the HITECH Act of 2009. This law led to a rapid rise in electronic medical record systems in US hospitals, which had previously been close to absent among non-VA hospitals. To investigate this further, we focused on four subsamples defined by whether or not each veteran’s modal hospital had adopted health IT, at the time of his ambulance ride, and similarly by whether or not each veteran’s modal hospital had joined an ACO. In each of these subsamples, we performed the same IV regression of the effect of transport to a veteran’s modal hospital. Results are shown in Table 6, Columns 1, 2, 4, and 5. We obtain all of these results after adding hospital fixed effects in the first-stage and reduced-form regressions in Equations (10) and (11), respectively. Results are qualitatively unchanged regardless of their inclusion. In Columns 3 and 6 of Table 6, we also perform regressions in the overall sample (described in Panel B of Appendix Table A.13). We maintain all of the interactions implicit in our subsample results except that we allow hospital group fixed effects to remain constant before and after adoption of health IT or an ACO. We do so with the following control function approach. First, we estimate a first-stage regression that interacts everything with adoption status, except for fixed effects for hospital groups, 𝑔 (ℎ (𝑖)), defined by whether a hospital ever adopts health IT or an ACO: 𝐷 𝑖𝑚 = ∑︁ 1 Adopted𝑖 = 𝑎
  𝑚 𝑚 𝑚 𝑚 𝑚 𝑚 𝑚 𝜋1,𝑎 𝑍𝑖𝑚 + 𝛾1,𝑎 𝑍 𝑖 + X0𝑖 𝛿1,𝑎 + 𝜁1,𝑧 (𝑖),𝑎 + 𝜉1,𝑔 (ℎ (𝑖)) + 𝜀 1,𝑖 . (A.28) 𝑎 ∈ {0,1} 𝑚 and include them in an interacted control-function We then take estimated first-stage residuals 𝜀ˆ1,𝑖 model: 𝑌𝑖 = ∑︁ 1 Adopted𝑖 = 𝑎
  𝑚 𝛽 𝑎 𝐷 𝑖𝑚 + 𝛾 𝑎 𝜀ˆ1,𝑖 + X0𝑖 𝛿 𝑎 + 𝜁 𝑧 (𝑖) ,𝑎 + 𝜉𝑔 (ℎ (𝑖)) + 𝜖 𝑖 . (A.29) 𝑎 ∈ {0,1} As with our other control-function regressions, we compute standard errors by 50 bootstrapped iterations, drawing samples by zip code blocks, with replacement. A.14 Figure A.1: Visual IV 28−day mortality .105 .1 .095 coeff. = −.045 (.018) N = 401,319, J = 1,217 .09 .05 .1 .15 Probability of VA hospital .2 .25 Note: This figure shows the visual IV plot corresponding to our baseline IV regression of the effect of the VA on 28-day mortality. For each bin of the instrument, which is the ambulance leave-out propensity to arrive at a VA hospital, we plot the mean 28-day mortality on the y-axis and the probability that the index patient arrives at a VA hospital on the x-axis. VA arrival predictions correspond to a first-stage regression in Equation (3), and mortality predictions correspond to a reduced-form regression in Equation (4). The best-fit line in the visual IV plot replicates the IV estimate of the effect of the VA on 28-day mortality, which we perform to obtain the standard error (in parentheses). This IV regression uses 401, 319 observations and 1, 217 combinations of ambulance company identifiers and Dartmouth Atlas Hospital Referral Regions (HRRs). The baseline sample selection is given in Appendix Table A.1. Controls include patient zip code dummies, ALS/BLS dummies, source of the ambulance ride, time categories, and patient prior utilization, which are detailed in Appendix Table A.2. A.15 −.1 −.08 Effect of VA −.06 −.04 −.02 0 Figure A.2: Combinations of Controls baseline controls 1 2 3 hold−out controls 4 5 6 7 8 Number of controls Mean estimate 9 10 11 12 Min/max estimates Note: This figure shows IV estimates of the VA effect on 28-day mortality on the y-axis, from Equation (2), varying the number of controls included in the IV regression. Numbered incremental controls correspond to categories or subcategories of variables that are presented in order in Appendix Tables A.2
and A.3. All specifications include the five baseline controls. Therefore, the figure represents 5 + 27 − 1 = 132 specifications. For each number of controls 𝑛 for 𝑛 > 5, we consider “7 choose 𝑛 − 5” specifications. The mean IV estimate is shown with a dashed line; the minimum and maximum IV estimates are shown with a short dashed line. We use our baseline sample, described in Appendix Table A.1. A.16 Figure A.3: Treatment Effects by Time and Sample −.06 OLS estimate −.04 −.02 0 A: OLS 7 52 104 156 208 260 312 364 Days All rides No ride in past 180d First ride No ride in past 30d No ride in past 365d −.06 −.04 IV estimate −.02 0 B: IV 7 52 104 156 208 260 312 364 Days All rides No ride in past 180d First ride No ride in past 30d No ride in past 365d Note: This figure shows mortality treatment effects over varying days since the ambulance ride and in varying samples restricting by prior rides. “Days” indicate one-week intervals from the ambulance ride. Panel A shows OLS results corresponding to Equation (6). Panel B shows IV results corresponding to Equation (5). The vertical dashed line indicates treatment effects on 28-day mortality, our baseline outcome. All regressions use a sample of ambulance rides with no prior ride in the last year. A.17 Figure A.4: Joint Inequality Constraints 0 5 Percent 10 15 A: No Mortality Displacement 10 22 34 46 Test statistic 58 test stat. = 29.8 crit. value = 41.9 0 5 Percent 10 15 B: No Negative Hazard Rate 0 25 50 Test statistic 75 100 test stat. = 4.3 crit. value = 72.7 Note: This figure shows the test statistic for joint inequality constraints and bootstrapped-generated distributions of the test statistic under the least favorable version of the null hypothesis. Panel A shows the joint inequality test of no mortality displacement, as defined by null hypothesis in Equation (A.7). Panel B shows the joint inequality test of no negative hazard rates, as defined by the null hypothesis in Equation (A.16). The test statistic for both tests is shown as a solid vertical line. The one-sided critical value, or 95th percentile of the bootstrapped distribution of the test statistic under the least favorable version of the null hypothesis, is shown as a dashed vertical line. Details of the test statistic and the bootstrap procedure for Panels A and B are given in Appendices A.2.2 and A.2.3, respectively. A.18 Figure A.5: Mean Hazard Differences Percent 10 15 5 0 0 5 Percent 10 15 20 B: VA vs. Non-VA Users 20 A: VA vs. Non-VA Compliers −.2 −.1 0 .1 .2 Difference (p.p.) difference = .022 std. err. = .078 −.02 .01 .025 .04 Difference (p.p.) difference = .059 std. err. = .006 Percent 10 15 5 0 0 5 Percent 10 15 20 D: Non-VA Compliers vs. Users 20 C: VA Compliers vs. Users −.005 −.1 −.05 0 .05 .1 .15 Difference (p.p.) difference = .055 std. err. = .048 −.2 −.1 0 .1 .2 Difference (p.p.) difference = .092 std. err. = .063 Note: This figure shows tests of equality of mean hazard rates for different sets of hazard rates, as defined by the null hypothesis in Equation (A.18). Each panel corresponds to a comparison between sets of hazards corresponding to VA or non-VA compliers or users. Details of the statistical procedure are given in Appendix A.2.4. Hazard rates for compliers are estimated by two-stage least squares and denoted in the appendix by ℎˆ 𝐼 𝑉 (𝑡; 𝑑), where 𝑑 = 1 for compliers assigned to the VA and 𝑑 = 0 for compliers assigned to a non-VA hospital. Hazard rates for users are estimated by OLS and denoted by ℎˆ 𝑂𝐿𝑆 (𝑡; 𝑑), where 𝑑 similarly denotes VA users (𝑑 = 1) vs. non-VA users (𝑑 = 0). The solid black line shows the test statistic, and the histogram shows the distribution of bootstrapped test statistics under the null hypothesis. Bootstrapped standard errors are given in the caption. A.19 Figure A.6: Joint Equality Constraints Percent 10 5 0 0 5 Percent 10 15 B: VA vs. Non-VA Users 15 A: VA vs. Non-VA Compliers 20 40 60 Test statistic 80 100 20 35 test stat. = 46.6 crit. value = 72.6 Percent 10 5 0 0 5 Percent 10 15 D: Non-VA Compliers vs. Users 15 C: VA Compliers vs. Users 50 65 80 Test statistic test stat. = 6219.200000000001 crit. value = 70.6 20 40 60 80 100 Test statistic test stat. = 110.5 crit. value = 72.3 20 45 70 Test statistic 95 120 test stat. = 85.5 crit. value = 72.9 Note: This figure shows tests of joint equality of hazard rates for different sets of hazard rates, as defined by the null hypothesis in Equation (A.19). Each panel corresponds to a comparison between sets of hazards corresponding to VA or non-VA compliers or users. Details of the statistical procedure are given in Appendix A.2.4. Hazard rates for compliers are estimated by two-stage least squares and denoted in the appendix by ℎˆ 𝐼 𝑉 (𝑡; 𝑑), where 𝑑 = 1 for compliers assigned to the VA and 𝑑 = 0 for compliers assigned to a non-VA hospital. Hazard rates for users are estimated by OLS and denoted by ℎˆ 𝑂𝐿𝑆 (𝑡; 𝑑), where 𝑑 similarly denotes VA users (𝑑 = 1) vs. non-VA users (𝑑 = 0). The solid line shows the test statistic, the histogram shows the distribution of bootstrapped test statistics under the null hypothesis, and the dashed line shows the one-sided 95th percentile critical value. A.20 Figure A.7: Marginal Treatment Effects .09 28−day mortality .095 .1 .105 A: Flexible Visual IV .05 .1 .15 Probability of VA hospital .2 −.15 Marginal treatment effect (MTE) −.1 −.05 0 .05 B: Marginal Treatment Effects .05 .1 .15 Probability of VA hospital .2 Note: This figure shows a flexible fit of the IV relationship between 28-day mortality and the ambulance propensity to transport to a VA hospital. Panel A shows the visual IV relationship with residual 28-day mortality on the y-axis and residual probability of being transported to a VA hospital on the x-axis. Both objects are residualized by baseline controls, described in Appendix Table A.2. The probability of being transported to a VA hospital is calculated from the first-stage relationship in Equation (3). The data underlying the fit in Panel A are similar to those in the linear visual IV plot in Appendix Figure A.1. The fit is based on five Gaussian basis splines. Panel B shows the implied marginal treatment effects, which are the analytical derivatives at each point on the fit in Panel A. 95% confidence intervals are calculated by 50 bootstrapped interations (drawn by zip codes, with replacement). Details are given in Appendix A.4. A.21