Uncertain Effects of Rosiglitazone on the Risk for Myocardial Infarction and Cardiovascular Death FREE

Nissen and Wolski (1) recently reported a meta-analysis of 42 clinical trials involving 27 847 patients that ignited a firestorm of controversy by concluding that treatment with rosiglitazone (Avandia, GlaxoSmithKline, Brentford, United Kingdom), a widely prescribed, peroxisome proliferator-activated receptor-γ agonist, was associated with an approximately 43% greater risk for myocardial infarction and an approximately 64% greater risk for cardiovascular death than placebo or other antidiabetic regimens. In performing their analysis, the investigators screened 116 phase 2, 3, and 4 trials. Of these, 48 met the predefined inclusion criteria of having a randomized comparator group and at least 24 weeks of drug exposure in all groups. Six of the 48 trials, with an unknown number of patients, were excluded because they did not report any cardiovascular events. Of the remaining 42 trials (38 double-blind and 4 open-label), only 10 assessed rosiglitazone monotherapy against placebo. Of the 32 trials comparing rosiglitazone with other antidiabetic therapy, 28 evaluated rosiglitazone versus placebo as an add-on therapy to sulfonylurea (n = 12), metformin (n = 10), insulin (n = 5), or usual care (n = 1), and 4 compared rosiglitazone monotherapy head-to-head with sulfonylurea or metformin. Thus, most of the trials were placebo-controlled.

The investigators acknowledged several limitations to their analysis. Misclassification and ascertainment errors were possible, because most studies were designed to assess end points other than cardiovascular disease. Study protocols had variable inclusion and exclusion criteria and drug dosing regimens. Overall event rates were low, partially because trial durations were relatively short, ranging from 24 to 52 weeks. Patient-level data were unavailable for time-to-event analysis. Relevant events, such as stroke or noncardiovascular death, were not reported, and whether reported death and myocardial infarction events were mutually exclusive was not always clear. In addition, the investigators did not present details of their literature search method apart from accessing published literature, trial registries, and U.S. Food and Drug Administration summary data. Without this systematic review context, the comprehensiveness of the analyzed data set is difficult to judge.

These matters aside, we scrutinize 2 additional limitations. First, study designs and populations were heterogeneous, yet data were pooled on the basis of a lack of statistical heterogeneity as assessed by the Cochran Q test. This test has limited ability to detect variation across studies with sparse data. We believe that the decision to pool all studies despite design and population heterogeneity probably led to artificial inflation and precision of the risk estimate. The investigators' own subgroup analyses, which were limited to the small trials alone or to the 2 large trials (DREAM [Diabetes Reduction Assessment with Ramipril and Rosiglitazone Medication] and ADOPT [A Diabetes Outcome Progression Trial]), did not demonstrate statistically significant associations (1). Furthermore, one might reasonably question whether results from the 3 trials that targeted patients with Alzheimer disease (n = 1) or psoriasis (n = 2) who did not have diabetes should be combined with results from other trials that included patients with diabetes or prediabetes. Because rosiglitazone is already contraindicated in patients with heart failure, one might also reasonably limit the assessment of risk to patients without that contraindication and not combine data from the single study in patients with diabetes who had congestive heart failure with data from other studies. Incidentally, this trial exhibited the highest number of myocardial infarctions (n = 5) and cardiovascular deaths (n = 3) among all the small trials in the rosiglitazone treatment group (1).

Second, a single methodological approach, the Peto fixed-effects model, was used to combine data. The authors justified this choice by the absence of statistically significant heterogeneity and the overall paucity of cardiovascular events, and they also referenced a simulation study by Bradburn and colleagues (2). This simulation exercise found that the Peto method performed well when event rates were rare and the numbers of patients in the study groups were balanced. In the meta-analysis at hand, several studies had major imbalances, whereby numbers of patients assigned rosiglitazone were 2 to 3 times greater than those of patients assigned the comparator. In such cases, the Peto method is reported to perform less satisfactorily (2–3), and alternative methods with a treatment group continuity correction, such as the Mantel–Haenszel method, and other approaches with and without continuity corrections merit consideration (3–6).

The methodological choices about what and how to combine are particularly salient when no events are seen in both the treatment and comparator groups (zero-total- event trials). The authors excluded 4 such trials from the myocardial infarction analysis and 19 such trials from the cardiovascular death analysis. It is common practice to exclude all zero-total-event trials from meta-analyses because they provide no information about the magnitude of the odds or risk ratios and do not contribute to producing a combined treatment effect greater or less than nil (2–3, 7). (Some specialized meta-analysis programs, such as the one used by Nissen and Wolski, do this by default.)

On the other hand, these trials may provide relevant information by showing that event rates for both the intervention and control groups are low and relatively equal (4–6). Including such trials can sometimes decrease the effect size estimate and narrow confidence intervals. Imagine a collective experience of 200 000 patients, equally divided into treatment and control groups, in which no events have been seen. Our best estimate of the event rate based on this experience is clearly less than 1 in 100 000. Imagine then that a single event is found in a subsequent trial with 100 patients. An analysis that ignored all the previous exculpatory information would estimate the risk to be 1%—at least 1000 times greater than it may actually be. Moreover, if we were to do a meta-analysis that ignored zero-total-event trials, the small trial would not be weighted in relation to all evidence available and would receive a larger weight than we would naturally assume.

We think that similar concerns about ignoring relevant data apply to trials exhibiting zero events in only 1 or the other study group (zero-event-trials). Consider the equation used to calculate the pooled estimate of the odds ratio according to Peto:

where O_i is the observed event rate in the treatment group, E_i is the expected event rate in the treatment group, and V_i is the variance of the difference (O_i – E_i) for the ith of k trials. According to this equation, the Peto odds ratio is inflated if the number of trials with zero events in the control group is greater than that of trials with zero events in the treatment group. In the data analyzed by Nissen and Wolski, this situation occurred with a ratio of 20:6 for myocardial infarction and 15:2 for cardiovascular death.

We reanalyzed the data set of 42 trials considered by Nissen and Wolski by various modeling and weighting methods using a meta-analytic software package called MIX (Meta-analysis with Interactive eXplanations [available at http://www.mix-for-meta-analysis.info]) (8). We estimated the pooled odds ratio as our measure of effect size by using fixed-effects (for example, Mantel–Haenszel) and random-effects (DerSimonian–Laird) models (8). When applicable, we used methods with or without 2 continuity corrections. One is a constant correction (CC) that adds values of 0.5 to all cells of the 2 × 2 contingency table of the study selected for correction. The other is a treatment arm correction (TAC) that adds values proportional to the reciprocal of the size of the opposite treatment group. (See the Appendix, for details.) The corrections were applied in 2 scenarios: Studies with zero events in 1 group and excluding studies with zero events in both groups (CC and TAC), and all studies with either zero events in either 1 group or both groups (CC+ or TAC+), effectively including all studies. Studies without zero events received no continuity correction.

Table 1 shows the pooled odds ratios and 95% CIs for analysis of all 42 trials. The odds ratios ranged from 1.43 to 1.26 for myocardial infarction and from 1.64 to 1.17 for cardiovascular death. Models without continuity correction yielded larger odds ratios than continuity-corrected models, with the CCs providing slightly lower estimates than the TACs. Although the odds ratios from these analyses were elevated, the CIs all contained an odds ratio of unity. Moreover, they suggest greater uncertainty than was reported in the original report but do not rule out the possibility that rosiglitazone increases risk for myocardial infarction or cardiovascular death.

We show pooled odds ratios for various subgroup analyses in Table 2. In general, the subgroup analyses exhibited similar odds ratios (except for the combined use of rosiglitazone with insulin, which exhibited higher odds ratios) but wider confidence intervals than did our primary analysis, consistent with the smaller sample sizes. None of these analyses conclusively adjudicate the association between rosiglitazone and the risk for myocardial infarction or cardiovascular death in particular groups of patients.

The controversy engendered by Nissen and Wolski's analysis caused the investigators of the large, ongoing RECORD (Rosiglitazone Evaluated for Cardiac Outcomes and Regulation of Glycaemia in Diabetes) trial to perform an unplanned interim analysis (9). This trial is designed as a noninferiority comparison of add-on rosiglitazone to metformin or sulfonylurea. The interim analysis showed a hazard ratio of 0.83 (95% CI, 0.50 to 1.36) for the adjudicated secondary end point of cardiovascular death and 1.17 (CI, 0.75 to 1.82) for the adjudicated secondary end point of myocardial infarction among the 4447 trial patients. On the basis of these interim results, the investigators concluded that there was no evidence of any increase in mortality rate but that data were insufficient to determine whether there was an increase in the risk for myocardial infarction (9). The statistical power of these comparisons was limited because of an unexpectedly low event rate and incomplete follow-up (a mean of 3.7 years instead of the planned median of 6 years), but the confidence intervals overlapped those reported in Nissen and Wolski's meta-analysis. This observation, along with a more than 30% excess risk for myocardial ischemic events in rosiglitazone-treated patients reported in the meta-analysis conducted by GlaxoSmithKline (10), lends continued support to those questioning the cardiovascular safety of rosiglitazone (11–12). A recent Cochrane review of 18 studies in patients with diabetes indicated a tendency toward increased risk for myocardial infarction with rosiglitazone treatment but could not confirm statistically significant differences in odds ratios for rosiglitazone versus controls (13). A large observational study in 33 363 patients did not show an increased risk for adverse cardiovascular outcomes in patients taking rosiglitazone compared with other therapies (14). Overall, these reports indicate confusing and sometimes conflicting results about cardiovascular risk associated with rosiglitazone therapy.

The risk for myocardial infarction and death from cardiovascular disease for diabetic patients taking rosiglitazone is uncertain. Neither increased nor decreased risk is established. Using the same data analyzed in a recent, widely publicized meta-analysis (1), we showed the fragility of effect sizes for these risks. We think that excluding trials with zero events in the index meta-analysis probably exaggerated risk estimates and that including these trials by applying continuity adjustments in this instance temper the exaggerated estimates.

Our analysis is restricted by the same limitations as those of the index analysis: short follow-up; low event rates; absence of patient-level data about time to event; variable and probably incomplete outcome ascertainment; and inability to reliably assess total mortality rate or composite outcomes, such as death or myocardial infarction. Neither analysis is a comprehensive systematic summary of all available evidence about the potential cardiovascular risks of rosiglitazone. We acknowledge that our analysis does not establish the amount of bias associated with different analytic methods for pooling trials with sparse events or with various choices of continuity corrections. We did not test other choices for continuity corrections. Lower correction values than those commonly used and applied in our analysis might cause less of a shift, whereas higher correction values would result in a greater shift toward a null effect (odds ratio of unity) compared with unadjusted pooled estimates.

In the end, we believe that only prospective clinical trials designed for the specific purpose of establishing the cardiovascular benefit or risk of rosiglitazone will resolve the controversy about its safety. In our opinion, available evidence does not justify what the authors of the original meta-analysis (as well as the media, the U.S. Congress, and worried patient groups) decried as an “urgent need for comprehensive evaluations” (1).

This Appendix describes the continuity corrections applied to myocardial infarction data for trial number 49653/04 in Nissen and Wolski's meta-analysis (1). The CC for continuity adds 0.5 to each cell of the 2 × 2 contingency table, effectively increasing the treatment and control group sizes by 1 and the total study sample size by 2 (from 348 uncorrected to 350 corrected). The TAC for continuity adds a value proportional to the reciprocal of the size of the opposite treatment group, normalized to a sum of 1 for event and no-event cells, resulting in an increase in the total study sample size by 2 (identical to that in the CC for continuity). With R being the ratio of group sizes and S being the sum of corrections for event and no event cells, the TAC for continuity adds a factor of R/S*(R + 1) to the larger group and 1/S*(R + 1) to the other group. In the example shown (Appendix Table), S is set to 1 and R is 232/116 = 2. The correction in the (larger) treatment group becomes 2/1*(2 + 1) = 2/3 = 0.67, and that in the (smaller) control group becomes 1/1*(2 + 1) = 1/3 = 0.33.