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Dr. Therese A. Stukel, Institute for Clinical Evaluative Sciences, 2075 Bayview Avenue, G106, Toronto, Ontario M4N 3M5, Canada
Randomized clinical trials (RCTs) and meta-analyses have shown substantial (14% to 24%) relative reductions in all-cause mortality over 1 to 2 years in patients with coronary artery disease randomized to cardiac rehabilitation programs (1). Women, elderly patients, low-income groups, and ethnic minorities tend to be under-represented in RCTs (1).
In this issue of the Journal, Suaya et al. (2) undertake the largest U.S. population-based study of all-cause mortality after cardiac rehabilitation among older patients with coronary disease. They studied 601,099 Medicare enrollees aged 65 years or older who were hospitalized with coronary disease or for cardiac revascularization in 1997 and survived 30 days after hospital discharge. Patients were followed for 5 years. Exposure to cardiac rehabilitation services was defined as receipt of at least 1 cardiac rehabilitation session within 1 year of discharge, with high users attending at least 25 sessions.
Their primary findings were a 21% to 34% relative decrease in 5-year mortality rates between users and nonusers, overall and across all clinical and demographic subgroups, but with higher short-term than long-term benefits. These findings generally provide evidence supporting the benefits of cardiac rehabilitation; however, the true effect size remains ambiguous.
Because this was an observational study, it is subject to potential biases (3). These include selection bias, whereby patients who are healthier, more motivated, better educated, and with better self-management skills attend and complete cardiac rehabilitation programs. Therefore, the lower mortality in cardiac rehabilitation users may be partly due to predisposing factors (confounders) that decrease their mortality, irrespective of cardiac rehabilitation services. Statistical adjustment may control for some of these differences, but only for measured and not unmeasured confounders. An often overlooked bias in observational studies is survival bias. Sicker patients may die before receiving treatment so that they are counted as both nontreated and deaths, leading to an overestimation of the benefits of treatment. These authors attempted to address both types of biases.
Propensity-based matching is an efficient technique to minimize differences in measured risk factors between treatment groups. The propensity score is the estimated probability of receiving the treatment of interest based on all measured patient risk factors. In this study, the probability of receiving cardiac rehabilitation was first modeled using multivariable logistic regression. The cardiac rehabilitation users (cases) were then matched to nonusers (controls) according to propensity to receive cardiac rehabilitation, excluding unmatched patients, so that matched pairs had the same probability of receiving cardiac rehabilitation. Propensity score methods are often not applied correctly. The criteria for assessing quality of propensity-matched studies suggested by Austin (4) were met in this study. The propensity score model and the matching method were explicitly described, the balance in the baseline covariates between matched groups was reported and compared using standardized differences rather than hypothesis testing, and the statistical analysis accounted for the matched nature of the sample.
By closely matching on propensity score and hard matching on other strong confounders, the authors simultaneously balanced multiple measured confounders. To attenuate survival bias, controls were required to survive the same interval between discharge and first use of cardiac rehabilitation as the matched case so that both had similar opportunities to receive cardiac rehabilitation services. The authors retained 70,040 matched pairs (96% of users, 13% of nonusers). Crude mortality in the matched control group was less than one-half that of the original sample (5.3% vs. 11.6%) so that controls were much healthier than the average nonuser; however, matching ensured that they were similar to users and were all potential candidates for cardiac rehabilitation. The authors compared mortality by computing observed 5-year survival for each matched pair and testing for differences using McNemar's 2 × 2 concordance test. To help with interpretation, the range of sessions attended by users should be reported.
In sensitivity analyses, they performed 2 analyses on the original study population. First, they analyzed mortality using probit regression models, adjusting for patient and hospital characteristics. They estimated each patient's adjusted absolute survival probability at 1 and 5 years, with and without cardiac rehabilitation services, aggregated to the group level and transformed to relative rates. This was a reasonable alternative to Cox models because there was no censoring and they analyzed 2 fixed time points.
Second, they used instrumental variable (IV) analysis to remove the effects of unmeasured bias (3). A valid IV fulfills 2 conditions: 1) it is correlated with treatment selection; and 2) it does not affect outcomes except through treatment so that it is not associated with measured or unmeasured risk factors. The IV behaves like a “natural randomization” of patients to “treatment groups” that differ in likelihood of receiving therapy. Unlike randomization, the difference in likelihood of receiving treatment across IV groups is not 100%, and one can explore but not prove that the groups are similar in unmeasured patient characteristics. A strong IV spans a wide range of treatment rates. Stronger IVs produce closer approximations to the average population effects from RCTs.
In this study, 2 geographic IVs were used, distance to cardiac rehabilitation facility from patient residence and state per capita supply of cardiac rehabilitation facilities. It is plausible that the IVs were related to the use of cardiac rehabilitation and that the measured risk factors were similar across IV levels, but reporting the baseline risk factors across IV levels would be useful for the reader. Providing supporting arguments for why unmeasured variables might be unrelated to the IVs would further reassure readers regarding their validity. Expressing the IV at a finer geographic level would produce a wider range of IV levels and a stronger IV. In summary, although the IVs in this study are likely valid, further supporting evidence could have been provided. The IVs may be weak, thereby reducing their potential to remove unmeasured bias.
Given these myriad issues, are the results plausible? Because 1- and 5-year mortality risks of the cardiac rehabilitation user and nonuser populations differ according to baseline risk, adjustment method, and subpopulation, the authors focused on relative effects. Benefits from the pair-matched analyses appear high (34% relative mortality reduction) given RCT results, in spite of optimal matching of measured risk factors. One would expect a more conservative result from defining cases based on receipt of a minimum of 1 cardiac rehabilitation session. In fact, Figure 1B of Suaya et al. (2) shows a smaller benefit (19% relative reduction) for high versus low users, a population in which the healthy user effect is presumably attenuated. IV analyses also appear more credible (21% relative reduction) but may be slightly optimistic if the IVs are weak. Thus, the overall benefits found were plausible, but the effect sizes may be overstated.
There are numerous sets of competing factors operating simultaneously when the net benefits of cardiac rehabilitation in RCTs and real-world populations are compared. Relative benefits of therapies in routine clinical practice are often lower than in clinical trials because they do not replicate ideal trial conditions with defined protocols and trained therapists implementing strategies to maintain compliance. Program delivery in routine practice is likely heterogeneous and may not implement the most current regimens of exercise, education, and lifestyle modification nor be delivered by interprofessional teams. Variations in effects may also arise from differences in motivational behaviors. These are likely biased in favor of greater effects in RCTs because compliance rates in general populations are often far lower than in RCTs, given healthy volunteer effects. It is therefore surprising to find stronger effects in general populations than in RCTs.
Because RCTs show that cardiac rehabilitation has long-term effects, one expects the 1-year benefits to be much smaller than the 5-year benefits. The fact that this is reversed casts doubt on the extent to which this is a pure cardiac rehabilitation rather than a healthy-behavior effect. To ensure that nonusers were healthy enough to have potentially received 1 year of services, restricting analyses, especially the dose-response analyses, to patients who survived 1 year post-discharge might attenuate the healthy-user effect.
A dose-response effect with respect to number of visits is important and was also found in other studies (5). This underscores the potential causal mechanisms of behavioral responsiveness, a major unexplained confounder that could not be adjusted for because there was no analogous compliance measure among controls.
Despite these issues, this was a well-designed, sophisticated study. It provides evidence that there is indeed a clinically important effect of cardiac rehabilitation in actual practice. We can debate whether the true size of the effect is 10% or 30%, but both are large when translated into absolute population numbers. The central issue becomes how to improve cardiac rehabilitation referral and compliance, given that fewer than 50% of patients access these programs even in publicly funded systems.
↵⁎ Editorials published in the Journal of the American College of Cardiologyreflect the views of the authors and do not necessarily represent the views of JACCor the American College of Cardiology.
- American College of Cardiology Foundation
- Suaya J.A.,
- Stason W.B.,
- Ades P.A.,
- Normand S.-L.T.,
- Shepard D.S.
- Austin P.C.