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Blood, 1 July 2002, Vol. 100, No. 1, pp. 366-367
CORRESPONDENCE
To the editor:
Cyclosporine modulation in poor-risk acute myeloid leukemia
The recent report from the Southwest Oncology Group by List et
al1 regarding the benefit of cyclosporine modulation of P-glycoprotein drug resistance in poor-risk acute myeloid leukemia (AML) was read with anticipation, as optimal regimens for this difficult patient population have remained elusive. Upon reviewing the
paper, however, several concerns became apparent. The use of one-sided analysis to determine superiority of the
cyclosporine arm was explained as follows: "the principal objective of the study was to assess whether [cyclosporine A] improves
treatment outcomes." 1(p3214) But the paper acknowledges
that the pilot study of cyclosporine modulation showed that
"treatment with CsA delayed the hepatic elimination of bilirubin
... resulting in reversible conjugated hyperbilirubinemia and
increased systemic anthracycline exposure" 1(p3212);
therefore it seems difficult to justify dismissing the possibility that
the cyclosporine arm could do worse than the control arm necessitating 2-sided analysis. This significant flaw in design diminishes the power of the study. This seems particularly important given that the primary end point of the study, increased complete remission (CR) rate with cyclosporine induction, was not
reached and that the conclusions reached by the authors are based
entirely on secondary and subgroup analysis. The most powerful conclusion from the study is that cyclosporine
modulation results in a significant improvement in the duration of
remission and in overall survival. But the use of stem cell transplantation for patients in remission is a potent confounding variable for each of these results. The authors accurately point out
that, among patients under age 60 who achieved CR, 9 of 25 (36%) of
patients in the control arm and 17 of 39 (43%) of patients in the
cyclosporine arm received stem cell transplantation. Comparison of the
percentages of eligible patients transplanted in each arm appears
tantalizingly similar. But an equally accurate manner in which to
present this data is that, in absolute numbers, 8 more patients in the
cyclosporine arm received transplantation. Although this number is
small, this represents nearly 7% of the patients randomized to the
cyclosporine arm and is nearly double the number of patients
transplanted in the control arm. This small number is pertinent given
that the basis of the significance favoring the cyclosporine arm at 2 years for relapse-free survival (RFS) in patients in CR and overall
survival for all patients is, in absolute terms, 8 patients and 9 patients, respectively. Whereas the authors provide some statistical
reasoning to support their conclusion that "the CsA effect was not
attributable to transplantation in remission," 1(p3215)
this significant conclusion warrants more detailed analysis. Who were
the patients that received transplants, and by what criteria was transplantation determined? What type of transplants did they receive? Was HLA matching similar between these groups? Was there transplantation-associated mortality? When dealing with such a small
number of patients, a factor as random as the availability of matched
siblings may dramatically affect the results. Combining the improper use of one-sided analysis and the confounding
effect of stem cell transplantation for patients in remission with a
small but real imbalance in pretreatment cytogenetics favoring the
cyclosporine arm, a clear conclusion that cyclosporine modulation has
significant long-term benefit does not seem capable of eliminating type
I error (ie, the probability of incorrectly concluding that there is a
statistical difference in a data set). Although this study clearly
shows that cyclosporine modulation in poor-risk AML results in a
significant decrease in residual disease following induction therapy,
the long-term significance regarding relapse-free survival and overall
survival appears to be a matter of speculation.
Jim V. Beattie and Paul J. Petruska
Correspondence: Jim V. Beattie , Department of Medicine,
Division of Hematology and Oncology, Saint Louis University, 3635 Vista
Ave, St Louis, MO 63110-2359; e-mail: beattiej{at}slu.edu
References
1.
List A, Kopecky K, Willman C, et al.
Benefit of cyclosporine modulation of drug resistance in patients with poor-risk acute myeloid leukemia: a Southwest Oncology Group Study.
Blood.
2001;98:3212-3220[Abstract/Free Full Text].
Response:
Benefit of cyclosporine modulation of drug resistance in
patients with 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 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 eliminated
MDR1-overexpressing clones in sequentially analyzed
relapse specimens.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(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.
Kenneth J. Kopecky, Alan
F. List, and Frederick R. Appelbaum
Correspondence: Alan F. List, The Arizona Cancer Center,
Bone Marrow Transplant Program, 1515 N Campbell Ave, Room 3945, PO Box
245024, Tucson, AZ 85724
References
1.
List A, Kopecky K, Willman, et al.
Benefit of cyclosporine modulation of drug resistance in patients with poor-risk acute myeloid leukemia: a Southwest Oncology Group Study.
Blood.
2001;98:3212-3220[Abstract/Free Full Text].
2.
List AF, Spier C, Greer J, et al.
Phase I/II trial of cyclosporine as a chemotherapy-resistance modifier in acute leukemia.
J Clin Oncol.
1993;11:1652-1160[Abstract/Free Full Text].
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Related Article in Blood Online:
-
Benefit of cyclosporine modulation of drug resistance in patients with poor-risk acute myeloid leukemia: a Southwest Oncology Group study
- Alan F. List, Kenneth J. Kopecky, Cheryl L. Willman, David R. Head, Diane L. Persons, Marilyn L. Slovak, Robert Dorr, Chatchada Karanes, Harry E. Hynes, James H. Doroshow, Muhammad Shurafa, and Frederick R. Appelbaum
Blood 2001 98: 3212-3220.
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