Gefitinib for recurrent non-small-cell lung cancer: all things are not created equal.

Two studies reported in this issue of Journal of Clinical Oncology have results in which the distributions of outcomes for patients with non–small-cell lung cancer treated with gefitinib were similar to those for standard chemotherapy treatment control arms using docetaxel and vinorelbine. The important question is to what extent these two studies provide evidence that the efficacy of gefitinib is similar to that of the chemotherapy-treated control arms. The report by Crino et al discusses a randomized phase II trial designed to determine superiority of gefitinib compared with vinorelbine for previously untreated elderly advanced non–smallcell lung cancer. They conclude in their discussion, “Although the present study was not designed to show equivalence between the two drugs, there was no statistical difference” between the two treatments. The report by Maruyama et al presents results from a randomized phase III trial that compared gefitinib with docetaxel in Japanese patients with relapsed non–small-cell lung cancer. This trial was originally designed as a superiority trial, but relevant data regarding the possible equivalence of gefitinib and docetaxel led the investigators to modify the design to target a noninferiority hypothesis. These studies prompt questions about the concordance of the clinical and statistical interpretation of the data, namely whether there is enough evidence from these two studies for clinicians to conclude clinical equivalence in outcomes of patients treated with the two agents. This issue is directly related to the design of each trial and whether additional studies are needed to formally address the statistical issue of noninferiority of gefitinib to standard of care, given that a soon to be published subsequent trial was designed to formally address noninferiority of gefitinib versus docetaxel in the same patient population as the Maruyama et al study. Although noninferiority designs are potentially important for regulatory approval, one wonders whether they are an efficient use of clinical resources or necessary for making clinical decisions. Unlike superiority trials, which aim to demonstrate that a novel treatment outperforms a standard regimen by a particular margin of superiority, noninferiority studies are appropriate for determining whether a novel agent is about as effective as the current standard, especially when the new treatment is less toxic. These studies specify a small noninferiority margin, which is the amount the new treatment can be less effective than the standard and still be considered an acceptable treatment, and test whether the difference between the standard and the new treatment is less than the specified noninferiority margin. In considering the magnitude of an acceptable noninferiority margin, the possible small reduction in efficacy must be weighed against the possible improvements in the safety profile, impact on the patient’s quality of life, cost, and other factors. This margin must also be less than the known magnitude of benefit of the standard treatment control arm because, otherwise, a conclusion of noninferiority would not be sufficient to establish that the new treatment was better than best supportive care (BSC). Consideration of the precision of estimates is crucial in the interpretation of noninferiority studies, and thus, the results can perhaps best be explained through CIs. If the two-sided CI around the point estimate of the primary end point includes the noninferiority margin, then the study does not establish noninferiority because the results do not rule out an unacceptably large decrease in efficacy. If the CI excludes the noninferiority margin (in favor of better outcomes with the new treatment), then it can be concluded that the new treatment is within an acceptable margin of the standard. Furthermore, superiority of the new treatment may be concluded if the CI excludes equal efficacy in favor of better outcomes on the new treatment. This approach differs from that used in the more common superiority trial, in which the null hypothesis of treatment equality is formally tested against an alternative hypothesis of superiority of the new treatment. With regard to the report by Crino et al, it is important to highlight that their conclusion of “no statistical difference” in treatments does not consider the precision of their estimates. Failure to reject the null hypothesis in a superiority trial is not the same as accepting the null hypothesis because there is always a range of possible null values that would not be rejected. The gefitinib versus vinorelbine overall survival (OS) hazard ratio was 0.98 (95% CI, 0.66 to 1.47). A noninferiority margin was not prespecified, but in this case, an unacceptably large noninferiority margin corresponding to a hazard ratio of 1.47, the upper bound of the reported CI, would be needed for the results to support a conclusion of noninferiority. This ratio corresponds to a 47% higher event rate with gefitinib. Because noninferiority margins are seldom prespecified in superiority trials, claims of noninferiority after failure to reject the null hypothesis in favor of superiority are problematic. The results of this study also do not provide strong indirect evidence of benefit from gefitinib relative to BSC because a previous study comparing vinorelbine with BSC in a similar population had an OS hazard ratio for vinorelbine versus BSC of 0.65 (95% CI., 0.45 to 0.93). Although the point estimate of 0.65 suggests that a ratio less than 1.53 (1:0.65) in the Crino et al study might be sufficient JOURNAL OF CLINICAL ONCOLOGY E D I T O R I A L VOLUME 26 NUMBER 26 SEPTEMBER 1