Mortality Among Hospitalized Medicare Beneficiaries in the First 2 Years Following ACGME Resident Duty Hour Reform FREE

Widespread concern about the number of deaths in US hospitals from medical errors¹ prompted the Accreditation Council for Graduate Medical Education (ACGME) to implement duty hour regulations effective July 1, 2003, for all ACGME-accredited residency programs.^2- 3 Work limitations for residents included no more than 80 hours per week, with 1 day in 7 free of all duties, averaged over 4 weeks; no more than 24 continuous hours with an additional 6 hours for education and transfer of care; in-house call no more frequently than every third night; and at least 10 hours of rest between duty periods.²

Although there is extensive scientific evidence linking fatigue and impaired cognitive performance,^4- 9 little empirical data guided the design of the duty hour regulations,^10- 11 and the design itself remains controversial,^12- 13 with contrasting views as to whether the duty hour rules adversely affect patient care,^14- 16 benefit patient care,¹⁷ or do not go far enough in limiting work hours for physicians in training.^18- 19 A necessary byproduct of the reform has been an increase in the number of handoffs between residents, which has led to concerns about the continuity of care postreform.^14- 16 Similar work hour reforms in New York State, implemented in 1989, were not associated with changes in mortality rates for patients with heart failure, myocardial infarction, or pneumonia,²⁰ or rates for several procedural complications, although higher rates of some types of complications were observed.^21- 22 A recent evaluation of the ACGME reform, potentially limited by its data source, suggested that improvements in mortality for medical but not surgical patients may have been associated with implementation of the reform.²³

Because of this, we studied the association between changes in the ACGME duty hour rules and mortality rates among Medicare patients hospitalized in short-term, acute-care US nonfederal hospitals. We compared trends in risk-adjusted mortality rates among more vs less teaching-intensive hospitals to examine whether mortality changed differentially among these groups following implementation of the rules. An accompanying article reports a complementary analysis among patients hospitalized within the US Veterans Affairs (VA) health care system.²⁴

Approval for this study was obtained from the institutional review boards of the University of Pennsylvania and The Children's Hospital of Philadelphia, Philadelphia, Pennsylvania.

The main outcome measure was death within 30 days of hospital admission for all patients admitted for acute myocardial infarction (AMI), stroke, gastrointestinal bleeding, congestive heart failure (CHF), general surgery, orthopedic surgery, or vascular surgery. The medical conditions were a subset of the Agency for Healthcare Research and Quality (AHRQ) Quality Indicators for which mortality was a relevant outcome. Although the AHRQ Quality Indicators use only in-hospital mortality, we examined any in-hospital or postdischarge deaths within 30 days of hospital admission, a measure that eliminates bias due to length of stay differences across hospitals or time.²⁵ For these study conditions, there is evidence that mortality varies substantially across institutions and that high mortality may be associated with deficiencies in the quality of care.^26- 28

All Medicare patients admitted to short-term, acute-care, general US nonfederal hospitals from July 1, 2000, to June 30, 2005, with a principal diagnosis of AMI, CHF, gastrointestinal bleeding, or stroke or with a diagnosis related group classification of general, orthopedic, or vascular surgery comprised the sample. The initial sample included 12 052 344 patients from 5736 acute care hospitals that contributed data for all 5 years within the 50 states or Washington, DC.

We excluded patients from hospitals that opened or closed during this period (9600 patients from 33 hospitals), that had fewer than 350 admissions in any year (40 756 patients from 1640 hospitals), that did not have Medicare Cost Report data (14 514 patients from 39 hospitals), or that were missing more than 3 months of data in the prereform period or 2 months worth of data in the postreform period (276 040 patients from 703 hospitals). Hospitals with fewer than 350 total admissions for all Medicare patients per year in any year (a mean of <1 admission per day across all conditions) were removed to screen out hospitals that may not have been acute care facilities as well as those that were so small that they were likely to yield unstable estimates if included in a fixed effects analysis.

We also excluded patients younger than 66 years (n = 1 562 532) to allow a 180-day lookback, which utilized information on secondary diagnoses coded in hospitalizations within the 180 days before admission for better risk adjustment; older than 90 years (n = 720 191), because the proportion of such patients that are treated aggressively may change over time in ways that cannot be observed well with administrative data; whose hospitalization spanned July 1, 2003 (n = 26 856); who were enrolled in a health maintenance organization at some point during the study period (n = 128 778); who had dates of death earlier than their discharge dates (n = 488); or who were transferred in from other hospitals (n = 13 615). Among patients with AMI or stroke, those patients discharged alive in fewer than 2 days (n = 50 926) were excluded because such cases may not represent actual AMIs or strokes.²⁸

So that each patient would only be represented once within each analysis, we defined an index admission as the first eligible admission between July 1, 2000, and June 30, 2005, for which there was no prior admission for the medical condition or surgical category within 5 years (using data back to July 1, 1995). We chose the first admission in the past 5 years for each patient to eliminate the possibility of selecting cases for which there would be a higher mortality rate postreform for reasons other than duty hour reform. Including multiple admissions for each patient in a longitudinal evaluation of a policy reform like this would be problematic because for patients with multiple admissions, any admission before the last was by definition an admission they survived. This means that an admission that resulted in death would be more likely to happen postreform, because the reform is confounded by the passage of time. Using only the first admission in the past 5 years excluded 678 453 patients, leaving a total sample for our analysis of 8 529 595 patients from 3321 hospitals.

More than 90% of patients with AMI, stroke, and vascular surgery had a first admission that met these criteria, as did more than 82% of patients with gastrointestinal bleeding, general surgery, and orthopedic surgery. For patients with CHF, 66% had only 1 admission over the 5-year period. We therefore tested the stability of this approach by also assessing the associations with duty hour reform for patients with CHF who experienced a second admission within 6 months of the first admission, which allowed inclusion of an additional 12% of patients with CHF.

The risk adjustment approach used was developed by Elixhauser et al.²⁹ The Elixhauser method used 27 comorbidities (excluding fluid and electrolyte disorders and coagulopathy, which should not be used in quality indicator risk adjustment)^30- 31 and has been shown to achieve better discrimination than alternative approaches.^32- 33 This was augmented with adjustments for age and sex. For surgical patients, we also adjusted for diagnosis related groups, grouping diagnosis related groups with and without complications or comorbidities into 1 variable. We performed a 180-day lookback, including data from prior hospitalizations, to obtain more comprehensive information on comorbidities than available by using the index admission alone.³⁴ A series of stability analyses was conducted to assess whether the substantive conclusions were unchanged.³⁵ For patients with AMI, these included additional adjustments for anatomic location of the AMI (International Classification of Diseases, Ninth Revision [ICD-9] codes: anterior 410.00-410.19, inferolateral 410.20-410.69, subendocardial 410.7x, other 410.80-410.99). For patients with stroke, this included assessment of whether adjustment for the proportion of hemorrhagic strokes affected the results.

Data on patient characteristics were obtained from the Medicare Provider Analysis and Treatment File (MEDPAR), which includes information on principal and secondary diagnoses, age, sex, comorbidities, and discharge status, including dates of death.³⁶ Data on health maintenance organization status were obtained from the denominator files obtained from the Center for Medicare and Medicaid Services (CMS). The number of residents at each hospital was obtained from the Medicare Cost Reports from CMS. Because funding for graduate medical education is tied to the number of residents within each hospital under Medicare, hospitals have a strong incentive to report complete data. Data from the American Hospital Association were used to identify hospitals that merged, opened, or closed during the study period.

The primary measure of teaching intensity was the resident-to-bed ratio, calculated at a defined point in time as the number of interns plus residents divided by the mean number of operational beds. The resident-to-bed ratio has been used as an approach to differentiate major teaching, minor teaching, and nonteaching hospitals in previous studies.^37- 39 In cross-sectional comparisons of quality of care in teaching and nonteaching hospitals, findings have been similar regardless of whether the resident-to-bed ratio or measures available through the American Hospital Association such as Council of Teaching Hospitals membership were used.⁴⁰ Teaching hospitals were defined as those hospitals with resident-to-bed ratios of more than 0; major and very major teaching hospitals were those hospitals with a resident-to-bed ratio of 0.250 to 0.599 and 0.60 or higher, respectively.

Resident-to-bed ratios are used by the CMS to calculate indirect medical education (IME) adjustments,⁴¹ supporting legitimacy of the use of the resident-to-bed ratio as a marker of teaching intensity. The IME is the additional amount Medicare pays teaching hospitals for patient care due to the higher costs of care provision in these hospitals. For example, the median IME amounts were much higher for very major teaching hospitals (resident-to-bed ratio, 0.600-1.090; IME, $15 000 894) compared with major teaching hospitals (resident-to-bed ratio, 0.250-0.599; IME, $8 878 650), minor teaching hospitals (resident-to-bed ratio, 0.050-0.249; IME, $1 911 228), very minor teaching (resident-to-bed ratio, >0-0.049; IME, $234 549), and nonteaching hospitals (resident-to-bed ratio = 0; IME, $0).

We used the resident-to-bed ratio as a continuous variable, which provided more power for assessing associations with implementing the duty hour rules than dividing hospitals into arbitrary categories.^42- 43 We held the resident-to-bed ratio fixed using the level in prereform year 1 so that any potential behavioral response to the reforms by hospitals (such as changing the number of residents) would not confound estimation of the net effects of the duty hour reform. Resident-to-bed ratios varied little over time. The mean changes from prereform year 3 to prereform year 2, and from prereform year 2 to prereform year 1, were both 0.02. Prereform year 3 included academic year 2000-2001 (July 1, 2000, to June 30, 2001); prereform year 2, academic year 2001-2002; prereform year 1, academic year 2002-2003; postreform year 1, academic year 2003-2004; and postreform year 2, academic year 2004-2005.

We used a multiple time series research design,⁴⁴ also known as difference-in-differences, to examine whether the change in duty hour rules was associated with a change in the underlying trend in patient outcomes in teaching hospitals, an approach that reduces potential biases from unmeasured variables.^45- 46 The multiple time series research design compares each hospital with itself, before and after reform, contrasting the changes in hospitals with more residents to the changes in hospitals with fewer or no residents, making adjustments for observed differences in patient risk factors. It also adjusts for changes in outcomes over time (trends) that were common to all hospitals. This design prevents bias from 3 possible sources. First, a difference between hospitals that is stable over time cannot be mistaken for an effect of the reform, because each hospital is compared with itself, before and after reform. Because of this, hospital indicators for fixed effects were used in the logistic model. Second, changes over time that affect all hospitals similarly (eg, technological improvements) cannot be mistaken for an effect of the reform. Because of this, year indicators were used in the logistic model. Third, if the mix of patients is changing in different ways at different hospitals, and if these changes are accurately reflected in measured risk factors, this cannot be mistaken for an effect of the reform because the logistic model adjusts for these measured risk factors.

Although the method of difference-in-differences offers these advantages, it has limitations. Any diverging trend in mortality over time for more vs less teaching-intensive hospitals that was already in progress or coincident with the initiation of the reform could be mistaken for an effect of the reform, although we tested extensively whether the prereform trends were similar in more and less teaching-intensive hospitals and adjusted for any observed underlying difference in prereform trends. Less teaching-intensive hospitals, including all nonteaching hospitals, served as the primary control group for more teaching-intensive hospitals because they were less affected by the duty hour reform but were subject to the same technological quality improvement imperatives, changes in market conditions, and Medicare-specific initiatives such as pay for performance. In addition, they are geographically diverse with large patient populations, and similar patient discharge data are available. Data from July 1, 2000, to June 30, 2003, were used as the prereform period and data from July 1, 2003, to June 30, 2005, were used as the postreform period.

The dependent variable was death within 30 days of hospital admission, using logistic regression to adjust for patient comorbidities, secular trends common to all patients (eg, due to general changes in technology), and hospital site where treated. The effect of the change in duty hour rules was measured as the coefficients of resident-to-bed ratio interacted with dummy variables indicating postreform year 1 and postreform year 2. These coefficients, presented as odds ratios (ORs), measure the degree to which mortality changed in more vs less teaching-intensive hospitals after adjusting for cross-sectional differences in hospital quality and general improvements in care. They were measured for each year separately because of the possibility of either delayed beneficial effects or early harmful effects. Conditions were assessed both individually and together as combined medical and combined surgical groups.

In the models, baseline mortality levels were allowed to differ between more and less teaching-intensive hospitals and were assumed to have a common time trend until implementation of the duty hour rules, after which the teaching hospital trend was allowed to diverge. To assess whether underlying trends in risk-adjusted mortality were similar in higher and lower teaching-intensity hospitals during the 3 years before the ACGME duty hour reform, a test of controls was performed. Parameters were added to the model for interactions between the resident-to-bed ratio and indicators for prereform year 2 and prereform year 1. A Wald χ² test was used to determine whether these interactions were equal to 0. A statistically significant test of controls suggested that teaching and nonteaching hospitals had a diverging trend in mortality in the 3 years prereform that could not have been caused by the reform. When such diverging trends were found by the test of controls, post hoc analyses were conducted in which postreform results were compared with the prereform year 1 as a baseline rather than using data from the entire 3-year prereform period.

To provide examples of the effect of being in hospitals with different degrees of teaching intensity, we converted the regression coefficients into estimated probabilities of mortality for an average patient by using the mean values for each of the covariates and replacing hospital indicators by the resident-to-bed ratio; the examples compared hospitals with resident-to-bed ratios of 1 and 0. We tested the stability of the medical and surgical results by (1) eliminating patients admitted to hospitals in New York State, due to earlier passage of the Libby Zion laws^20- 21; (2) eliminating patients admitted from nursing homes, because such patients may not have been treated aggressively; (3) testing the robustness of the results to analysis without comorbidity adjustment to determine whether changes in the rate of coded comorbidities could explain any of these effects; and (4) examining the degree to which mortality changed in patients with a second CHF admission within 6 months of the first. All P values were either 2-tailed or, for χ² tests, multitailed. P<.05 was considered statistically significant. All statistical analyses were conducted with SAS version 9.1 (SAS Institute Inc, Cary, North Carolina).

The number of admissions for each of the conditions was fairly constant over time, differing by less than 10% per year for any condition (Table 1). Approximately 69% of the hospitals were nonteaching hospitals and approximately 9.2% of hospitals (treating 14.0% of patients) were major or very major teaching hospitals (Table 2).

Between prereform year 2 and prereform year 1, unadjusted mortality rates for the combined medical group increased in the very major teaching-intensive hospitals more than in other hospitals; however, mortality subsequently changed at similar rates from prereform year 1 to postreform year 2 (Figure 1). The test for controls for stroke indicated that in the 3 years before the reform, stroke mortality had diverged significantly in more vs less teaching-intensive hospitals (Wald χ² test, 12.0; P = .003); therefore, post hoc analyses were conducted that examined the associations without stroke separately. Unadjusted mortality for the combined medical group excluding stroke changed at similar rates for patients in hospitals of differing teaching intensity between 2000 and 2005 (Figure 1). This indicates that the prereform divergence was largely due to the changes in stroke mortality. Compared with nonteaching hospitals, hospitals with a resident-to-bed ratio of 1 had no change in the unadjusted odds of mortality for combined medical conditions in postreform year 1 (OR, 1.03; 95% confidence interval [CI], 0.99-1.08) or postreform year 2 (OR, 1.04; 95% CI, 0.99-1.09).

Among surgical patients, there was a relative increase in unadjusted mortality among patients in more teaching-intensive hospitals from prereform year 3 to prereform year 1, following which mortality in all hospitals declined to a similar degree (Figure 2). Compared with nonteaching hospitals, hospitals with a resident-to-bed ratio of 1 had no change in the unadjusted odds of mortality for combined surgical categories in postreform year 1 (OR, 1.04; 95% CI, 0.97-1.11) or postreform year 2 (OR, 0.99; 95% CI, 0.93-1.07).

In adjusted analyses of both the combined medical and combined surgical groups, there was no evidence of relative increases or decreases in the odds of mortality for patients in more vs less teaching-intensive hospitals in either postreform year 1 or postreform year 2 (Table 3). Results remained nonsignificant when the 2 postreform years were combined into a single resident-to-bed ratio × postreform coefficient.

None of the individual conditions other than stroke showed any significant relative changes in mortality in more vs less teaching-intensive hospitals in either postreform year 1 or postreform year 2. There was a statistically significant increase in mortality for patients with stroke in more teaching-intensive hospitals in postreform year 1 (OR, 1.08; 95% CI, 1.00-1.16; P = .04) and postreform year 2 (OR, 1.08; 95% CI, 1.01-1.16; P = .03) relative to less teaching-intensive hospitals (Table 3). Because of the prereform divergence for stroke mortality, an analysis was conducted in which the referent group was changed from the entire prereform period to prereform year 1 only. This indicated no relative increase in mortality, with the OR for postreform year 1 of 0.98 (95% CI, 0.90-1.08) and the OR for postreform year 2 of 0.99 (95% CI, 0.91-1.08). Analysis of the combined medical group excluding stroke showed no significant association of changes in mortality with teaching status (Table 3).

The test of controls was consistent with divergent prereform trends for the stroke (P = .003), combined medical conditions (P = .048), general surgery (P = .01), and combined surgical categories groups (P = .02). Except for stroke, there was no significant differential change in the odds of mortality in more vs less teaching-intensive hospitals after adjusting for the differential prereform trends for combined medical conditions. Using prereform year 1 as the referent period for each of these groups, there were no significant associations between the degree of change in mortality and teaching intensity between prereform year 1 and either postreform year 1 or postreform year 2.

Excluding patients admitted to hospitals in New York State or patients admitted from nursing homes from the statistical analyses did not change the results. We also examined whether changes in the coding of comorbidities could explain any of these effects. There was only a 0.7% relative decrease in the mean number of comorbidities in more teaching-intensive hospitals relative to nonteaching hospitals from prereform year 1 to postreform year 2, and sensitivity analyses without adjustment for comorbidities produced similar results. For example, the OR for combined medical conditions without risk adjustment was 1.03 (95% CI, 0.99-1.08) vs 1.03 (95% CI, 0.99-1.08) with risk adjustment. There also were no significant differences in the degree to which mortality changed in more vs less teaching-intensive hospitals for patients with CHF who had a second admission within 6 months of the first, in patients with AMI when additional adjustments for anatomic location were added, or in patients with stroke when adjustment for the proportion of hemorrhagic strokes was added.

To illustrate the magnitude of the changes in mortality associated with duty hour reform, we estimated the adjusted risk of mortality in each academic year for a hypothetical person with mean values of all regression covariates at 2 hypothetical hospitals: a nonteaching hospital (resident-to-bed ratio of 0) and a highly teaching-intensive hospital (resident-to-bed ratio of 1). In the combined medical group, mortality in a hospital with a resident-to-bed ratio of 1 did not change (9.06% in prereform year 1 vs 9.06% in postreform year 2), while in a hospital with a resident-to-bed ratio of 0 mortality decreased from 9.48% to 9.06%, a comparative increase of 0.42 percentage points (4.4% relative increase). For a patient representing combined surgical categories, mortality in a hospital with a resident-to-bed ratio of 1 decreased from 1.67% in prereform year 1 to 1.56% in postreform year 2, while in a hospital with a resident-to-bed ratio of 0 mortality decreased from 2.10% to 1.94%, a comparative increase of 0.05 percentage points (2.3% relative increase). None of these changes were statistically significant.

Implementation of the ACGME duty hour rules was arguably one of the largest efforts ever undertaken to reduce errors in teaching hospitals. The results of this study suggest that after 2 years it has not been associated with a significant positive or negative change in mortality among Medicare patients. These results should be considered in the context of 3 other studies.

First, the Healthcare Cost and Utilization Project's (HCUP’s) Nationwide Inpatient Sample (NIS) was the data source for a study by Shetty and Bhattacharya²³ that found a small but statistically significant relative improvement in mortality outcomes for medical but not surgical patients in teaching compared with nonteaching hospitals following duty hour reform. However, there are a number of potential limitations in these data. The HCUP NIS samples different hospitals in different years, as well as hospitals from different states in different years⁴⁸; therefore, analyses using these data could be biased by changes in the distribution of sampled patients across hospitals between the prereform and postreform periods. The study by Shetty and Bhattacharya²³ was also limited to the 551 hospitals included in the NIS both before and after reform. In contrast, our study, which includes Medicare data on 3321 hospitals, incorporates data from all hospitals in all years, allowing for more reliable testing for differences in outcomes before and after reform within the same hospital. There are no patient identifiers in the HCUP NIS, so that the data cannot distinguish between a single admission from different patients vs multiple admissions from the same patient. Inclusion of multiple admissions could make it appear that duty hour reform reduced mortality if the percentage of patients with multiple admissions was higher at nonteaching hospitals than at teaching hospitals. Because the HCUP NIS does not include information on out-of-hospital deaths, it was necessary for Shetty and Bhattacharya to use in-hospital mortality as the primary outcome. In-hospital mortality can change without any change in total mortality rates if patients are discharged faster or slower; discharge rates may have been influenced by the duty hour reform. Our study used 30-day (from admission) mortality, which is not affected by discharge patterns.

Second, a single-site study by Horwitz et al⁴⁹ compared changes in outcomes on the teaching vs nonteaching service before and after duty hour reform. It found no changes in length of stay, 30-day readmission rates, or adverse drug-drug interactions but did not have sufficient power to compare changes in mortality.

Third, we applied methods similar to those used in the present study to the population of patients receiving care in the VA health care system.²⁴ That study may be considered complementary to the present study because in aggregate VA hospitals are the largest site of residency training in the United States, whereas the vast majority of US patients are treated in non-VA hospitals. The VA study found improved mortality for medical patients in more teaching-intensive environments in postreform year 2, although among surgical patients, there were no relative changes for patients in more vs less teaching-intensive hospitals. The finding of reduced mortality for VA medical patients but not Medicare medical patients could reflect that the mean resident-to-bed ratio among VA teaching hospitals is much higher than in non-VA teaching hospitals and that residents may have more autonomy at VA hospitals,^50- 51 both of which could amplify positive or negative effects of the duty hour rules. Resident staffing models and clinical volume at VA hospitals may be different from non-VA hospitals of similar teaching intensity, which could enable higher rates of compliance with duty hour rules at VA hospitals. The lack of significant improvement in mortality among Medicare medical patients in higher teaching-intensity hospitals could reflect a different balance between the effects of decreased fatigue^18- 19,22 and worsened continuity^21,52 compared with VA hospitals. Observational studies may always have unmeasured confounders, which could have existed to a greater or lesser degree in the VA analysis than in the Medicare analysis.

Although we found a relative increase in mortality in patients with stroke in higher teaching-intensity hospitals postreform, this increase was not present when the referent group was prereform year 1. Because a relative increase occurred before reform, it is likely that this finding reflects a trend that was independent of duty hour changes. The reasons for this prior trend are not clear.

Coding of comorbidities changed at similar rates in all hospitals over time, with a relative decrease of 0.7% in the mean number of comorbidities in the most teaching-intensive hospitals relative to nonteaching hospitals in postreform year 2. The similarity of our results with and without comorbidity adjustment suggests that there were no major changes in the patient profiles over time for hospitals of different teaching intensity, that our results would likely be robust to the specific method of comorbidity adjustment chosen, and that changes in coding frequency do not explain the measured effects.

The absence of a relative change in mortality among Medicare beneficiaries in more teaching-intensive hospitals may reflect many factors. Lack of compliance with the duty hour rules has been described, although such surveys have been limited to self-reported compliance based on a potentially nonrepresentative sample of about 7% of all interns⁵³ or data collected by the ACGME.⁵⁴ There are strong financial incentives for residency programs to comply to avoid loss of accreditation. Even if programs are not in complete compliance, it seems likely that there has been a reduction in work hours that would be greatest in the subspecialties (eg, surgery) in which residents worked the most hours prereform. However, unless the appropriate resources were put in place at the institutional level to mitigate the impact of residents working fewer hours, the effect of duty hour reform at the local level would likely be to increase work intensity, which could offset potential benefits of decreased fatigue. Investigators in New York State examined the effects of the Libby Zion laws on mortality but found no differences in mortality in teaching vs nonteaching hospitals²⁰ or within the same teaching hospital.²¹ However, compliance rates were extremely low,^20,55 and thus the applicability of these studies to the ACGME duty hour rules is unclear.

There are several possible limitations to our study. We focused on one outcome, mortality. Although the duty hour rules were an attempt to reduce deaths from medical errors, measurement of other outcomes such as patient safety indicators may help to explain the relative effects of decreased continuity of care compared with decreased resident fatigue.

We do not have information on actual hours worked at each hospital. Our study may be considered an effectiveness study, in contrast with an efficacy study, because we measured the outcomes associated with the duty hour rules as implemented. Even with the size of the Medicare population, some of the CIs are still somewhat broad and we cannot rule out small and possibly clinically meaningful effects. This is particularly true for the individual condition analyses and for surgical patients because mortality was lower for surgical patients than for medical patients.

Any observational study is susceptible to unmeasured confounding. We used administrative data, so risk adjustment is more limited than with clinical data; however, by comparing outcomes over time within each hospital in more vs less teaching-intensive hospitals, potential bias from unmeasured cofounders is markedly diminished. Given the multiple time series difference-in-differences approach, to be a confounder a variable must have a differential rate of change in more vs less teaching-intensive hospitals. Because we adjusted for different baseline rates of change in more and less teaching-intensive hospitals, confounding would only occur if the prevalence of unmeasured risk factors changed at different rates according to hospitals' teaching intensity.

In conclusion, we found that implementation of duty hours limitations was not associated with any significant change in risk-adjusted mortality among Medicare patients. These results do not address whether the current design of duty hour rules is optimal,¹³ as other work has found significantly lower rates of errors with 16-hour vs 24-hour to 36-hour shifts.^18- 19 Given the lack of evidence of improvements in outcomes in this study, research should focus on examining different approaches to duty hour design as well as measuring resident work intensity and clinically relevant patient outcomes in addition to mortality.