Cyclosporine modulation in poor-risk acute myeloid leukemia

We thank Drs Beattie and Petruska for their comments and questions concerning our manuscript that raise important points relevant to all trials in patients with high-risk leukemia.1-1 The letter raises 2 issues regarding the design and analysis of the study. The first concerns the study's underlying hypothesis, that the addition of cyclosporin A (CsA) to a regimen of daunorubicin (DNR) and high-dose cytarabine would improve treatment outcomes. The prior experience with CsA provided adequate justification for optimism that adding CsA would have a net benefit. In the phase I/II trial performed in patients with poor-risk AML, coadministration of CsA and infusional daunorubicin yielded a high rate of complete remission and consistently eliminatedMDR1-overexpressing clones in sequentially analyzed relapse specimens.1-2 More importantly, dose-limiting toxicity was not encountered, despite the fact that CsA delayed the hepatic elimination of bilirubin and daunorubicin. Generally, one-sided design and analysis are appropriate for phase III studies that investigate the effect of adding an agent to a standard regimen, since the ultimate clinical recommendation is inherently one-sided: if there is evidence that adding the agent is beneficial, then its use may be recommended. Otherwise, the agent should not be added, and whether it has no effect or is detrimental is immaterial to this recommendation.

The possibility that the CsA arm might “do worse” was not, as the letter alleges, “dismiss[ed]” by the design or analysis of the study. The stated principal objectives of the trial included comparison not only of induction response and survival but also of the toxicity of the 2 regimens. In addition, the study's protocol required that the planned interim analyses include assessments of whether the study should be terminated early due to evidence against a clinically meaningful benefit from CsA, a much easier condition to satisfy than evidence of worse outcomes with CsA, which a 2-sided design would have required.

The assertion in the letter that designing the study to achieve an inherently one-sided objective “diminishes the power of the study” is rather misleading. For any given one-sided alternative hypothesis, that is, for any given magnitude of CsA benefit, a one-sided comparison has greater statistical power than the corresponding 2-sided comparison based on the same sample size and critical level. Therefore, employing a 2-sided test when a one-sided test is appropriate in fact “diminishes” statistical power. In other words (and we assume this is the authors' intended point), a 2-sided design requires a larger sample size than a one-sided design in order to have equivalent statistical power to detect any given magnitude of CsA benefit. This is indeed true but is simply a consequence of the fact that the objective of the study determines its design (including sample size). Requiring a 2-sided study's sample size when a one-sided design is appropriate prolongs the duration of the study and delays the availability of clinically important information.

The second issue raised in the letter concerns the role of stem cell transplantation. The analysis reported in the paper1-1 ^(p3215) was performed to investigate a specific question: whether the apparently beneficial effects of CsA might be attributable to an increased likelihood of receiving stem cell transplantation in remission. The letter requests “more detailed analysis” of the characteristics of the transplants and patients who received them. It is ironic that the authors criticize the use of “secondary and subgroup analysis” in one paragraph and then call for a much more extreme form of such analysis in the following paragraph. Any attempt to attribute differences in outcomes to differences in events following randomization, which is of course not based on protocol-directed “intent-to-treat” comparisons, is subject to unquantifiable biases. Our analysis of the impact of transplantation is certainly subject to this criticism, and we were therefore careful to claim only that the results “suggest[ed] that the CsA effect was not attributable to transplantation in remission.”^1(p3215)

The requested “more detailed analysis” is an attempt to identify these biases but is doomed to inconclusiveness. The decision as to whether or not a patient receives a transplant of a given type is the result of a complex balance of the expectations, experiences, resources, and preferences of the physicians, the patient, and even the patient's family and friends. The decision process is highly individualized, quite possibly differing according to prognosis and/or between treatment arms, and is largely undocumented. Therefore the question, which addresses a non-protocol-directed decision (ie, “Who were the patients that received transplants and by what criteria was transplantation determined”), cannot be answered with sufficient detail and confidence to ensure that the possibly large biases are all accounted for.

In addition, the authors make a strong argument against the very analysis they request, by emphasizing that “[w]hen dealing with such a small number of patients, … [small, uncontrolled effects] … may dramatically affect the results.” This is certainly true of any attempt to try to identify biases arising from the decision processes that led to transplantations in only 26 patients.

Finally, we note that the letter incorrectly implies that complete remission (CR) rate was the sole primary end point of the study. In fact, as described above, overall survival and toxicity were also primary end points of the study.