Changes in Hospital Mortality Associated with Residency Work-Hour Regulations

Context The health effects of regulations restricting housestaff work hours to 75 hours per week are largely unknown. Contribution The authors measured inpatient mortality of 1268738 patients admitted to 551 hospitals with medical diagnoses and 243207 patients admitted for surgical diagnoses before and after 2003, when the work-hour regulation took effect. After 2003, the mortality rate for medical patientsbut not surgical patientsdecreased more in teaching hospitals than nonteaching hospitals. Caution The authors classified a hospital as teaching if it had a residency program; however, some teaching hospitals have nonteaching patients. Implication Limiting residents' work hours was associated with lower in-hospital mortality rates for medical patients in teaching hospitals. The Editors For more than 20 years, the Accreditation Council on Graduate Medical Education (ACGME) and other observers have been concerned with excessive resident duty hours (19). The ACGME imposed national restrictions on duty hours in 1987, New York State enacted hours restrictions in 1989, and the ACGME's Residency Review Committee for Internal Medicine adopted duty-hour limits in the 1990s. Despite these regulations, enforcement before 2003 was not stringent and excessive resident work hours were common. In part to avoid federal legislation, the ACGME approved new resident duty-hour regulations that became effective on 1 July 2003 (1). The regulations limited resident workweeks to 80 hours or fewer and limited continuous duty to 24 hours, with 6 additional hours for transfer of care. The effect of these regulations is uncertain. An hours cap might reduce errors and mortality due to resident weariness. Alternatively, they might increase errors if they disrupt the continuity of patient care. Scholarly work on this question has been limited, and the conclusions of these studies were mixed. One study found that New York State's regulations did not affect mortality in patients who were admitted for pneumonia, congestive heart failure, or acute myocardial infarction (10). However, duty-hour violations were still common during the study period, making the results less relevant to current regulations. Another study indicated that interns working under a duty-hours cap made fewer errors than did a similar group under a traditional call system (6). This finding suggested that duty-hours caps improve patient outcomes, but the sample size was too small to show effects on mortality. The regulations may not have altered outcomes if residency programs did not change working conditions. However, the official ACGME report and multiple program director surveys documented major changes in work hours in residency programs after July 2003 (2, 1116). In addition, an independent survey reported that interns' average weekly work hours decreased from 70.7 to 66.6 hours despite widespread violations (5). We retrospectively analyzed discharge data collected between 2001 and 2004 to determine whether the ACGME regulations were associated with changes in inpatient mortality. Unlike previous work, our study has the statistical power to detect small effects because we used a large, nationally representative data set with patients from nonteaching hospitals as a control group. Methods Data Sources We used the Nationwide Inpatient Sample (NIS) from the Healthcare Cost and Utilization Project to assemble a nationally representative data set of hospital patients between 2001 and 2004. The NIS sampled approximately 20% of all community hospitals in the United States and included at least 7.4 million discharges annually since 2001. The NIS provided clinical and demographic information on each discharged patient, including age, sex, 10 diagnoses (1 principal and 9 secondary), principal procedure, month of admission, and income quartile of the patient's ZIP code. The NIS coded procedures and diagnoses according to the International Classification of Diseases, Ninth Revision. The study was exempt from approval by the Stanford University institutional review board because all patient-level NIS data were publicly available and deidentified. We used data from the American Medical Association to assign teaching status and calculate the number of residents for each hospital (4, 1721). Selection of Patients Before beginning our analysis, we selected principal diagnoses and procedures that represented a broad variety of medical and surgical diagnoses, were associated with high mortality rates, and were common in both teaching and nonteaching hospitals. Using these criteria, we selected 20 medical diagnoses and 15 surgical diagnoses. Patients with these diagnoses made up 34% of the total number of deaths in the sample and 13% of the patients (Table 1). We classified patients as surgical if their principal procedure code represented a major surgery and as medical if their principal diagnosis corresponded to a major internal medicine diagnosis. In addition, patients who were admitted for medical diagnoses but later had major surgeries during the same hospitalization were classified as surgical patients. Table 1. Included Diagnoses* We excluded populations with low mortality rates (including all pediatric and obstetric patients) because we lacked the statistical power to detect a significant effect in these groups. We also excluded patients transferred from other hospitals or correctional facilities. We assigned teaching status to hospitals by linking American Medical Association data on residency programs to NIS data on hospitals by using American Hospital Association identification numbers. We therefore excluded patients from states that did not permit the release of hospital identifiers (roughly 35% of the NIS). To create similar pre- and postregulation populations, we limited our final sample to patients from hospitals that admitted at least 100 patients both before (January 2001June 2003) and after (July 2003December 2004) the regulations were implemented. Assignment of Teaching Status and Regulation Period Teaching status is a critical variable in our analysis. The NIS classified patients as teaching if the admitting hospital had any type of educational program. For example, the NIS teaching variable would have erroneously classified surgical patients at teaching hospitals as teaching, regardless of whether their primary providers were residents (under the supervision of attending physicians) or attending physicians (with little or no resident involvement). To reduce this error, we first classified all patients in each hospital as internal medicine, general surgery, urology, or orthopedics patients on the basis of their principal diagnosis. We then classified patients as teaching if the hospital had a corresponding internal medicine, general surgery, urology, or orthopedics residency program (based on American Medical Association records). In addition, in hospitals with family practice programs, we classified internal medicine patients as teaching. For example, if a hospital had an internal medicine residency program, we analyzed all patients admitted for medical diagnoses as if they were admitted to a teaching hospital. Conversely, if the same hospital lacked a surgical residency program, we analyzed all patients admitted for surgical diagnoses as if they were admitted to a nonteaching hospital. In our model, hospitals could admit a mix of teaching and nonteaching patients depending on the hospital's mix of sponsored residency programs. However, all patients with the same diagnosis in one particular hospital would be analyzed as teaching or nonteaching unless the hospital gained (or lost) a residency program from one year to the next. With this procedure, misclassification of patients is still possible if a hospital has parallel teaching and nonteaching services. We later discuss the effect of misclassification on the interpretation of our results. Statistical Analysis We used a multivariate logistic regression model to estimate the changes in mortality associated with the regulations. Changes in nonteaching hospitals after July 2003 were unrelated to the regulations and therefore reflected underlying trends. Thus, changes that occurred in nonteaching hospitals act as a control for the changes associated with regulations in teaching hospitals. To derive our estimate, we subtracted the mortality trend in the control group (patients from nonteaching hospitals) from the mortality trend in patients from teaching hospitals. This method has been previously described in the economic and medical literature as a difference-in-differences approach (2224). We accounted for case-mix differences by adjusting each of our regression estimates for admitting diagnosis and all previous medical conditions included in the Charlson index except uncomplicated diabetes and peptic ulcer disease (25, 26). We included age in the regression along with indicator variables for sex, race, insurance status, year and month of admission, income quartile of the patient's ZIP code, and emergency admission. Hospitals also have very different patient populations and staffs, which cannot be observed by using available data. We tested several models to address these differences. We tried a generalized linear mixed model, but a Hausman specification test revealed that the basic assumptions underlying this model were not met (27). We therefore used a logistic regression model that treated each hospital's unobserved effect as a distinct intercept. Estimation of several hundred variables (one for each hospital) can lead to inconsistent estimates, but we reduced this problem by including only hospitals with more than 200 study-eligible patients (28). In addition, we compared our results to those from a conditional logistic regression model (which does not require the estimation of multiple intercepts). We found similar odds ratios in both, but we elected against using a conditional logistic regression model because the