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Randomized Clinical Trial of an Implantable Drug Delivery System Compared With Comprehensive Medical Management for Refractory Cancer Pain: Impact on Pain, Drug-Related Toxicity, and Survival

Operative Unit of Rehabilitation and Palliative Care, National Cancer Institute of Milan, Milan, Italy

To the Editor: In the October 1, 2002, issue of the Journal of Clinical Oncology, Smith et al¹ reported a randomized clinical trial carried out to evaluate the effectiveness of implantable intrathecal drug delivery systems (IDDSs) with comprehensive medical management (CMM) compared with CMM alone in the management of refractory cancer pain. The authors concluded, "IDDSs improved clinical success in pain control, reduced pain, significantly relieved common drug toxicities, and improved survival in patients with refractory cancer pain."

Unfortunately, this study brings up clinical, methodological, statistical and, above all, ethical issues, because of the emphasis given to the discussion of the results described, which really were borderline in both groups.

From a clinical point of view, it is not clear why the performance status of both groups of patients was not collected; nor was it clear how many patients were still undergoing anticancer treatment. Given that "In the CMM group, 15 patients died before the first evaluation (4th week) in respect to eight patients of the IDDS group," the doubt arises that, notwithstanding randomization, the CMM patients were more ill in respect to the IDDS group.

It also is unclear why 12 of the 101 IDDS randomly assigned patients "missed visits." What happened to these patients? Why did they miss their visits even though their pain was uncontrolled?

The authors reported that "data were recorded at baseline; at 2, 4, 6, 8, 10 and 12 weeks; and then monthly through 6 months." Why were the results of a longitudinal analysis, including all follow-up evaluations, not presented? It would have been much more clinically interesting. We cannot understand the data relating to the time to achieve analgesia in the two groups. Moreover, according to the authors, "the time point 4 weeks after randomization was chosen because rapid improvement in symptoms was deemed a necessity for terminally ill patients." From a clinical point of view, 4 weeks is a long time to evaluate and re-evaluate pain and toxicity , as well as to titrate the dosages of analgesics.

Moreover, the authors note that "a successful screening trial of intrathecal morphine was required before IDDS implant. Trial method consisted of epidural injection, epidural infusion, intrathecal injections, or intrathecal infusion. Then pumps were implanted as soon as practical after the trial of intraspinal morphine." The authors use the terms "intrathecal" and "intraspinal" interchangeably. Although the former means the placing of the catheter in the intrathecal space, the latter also includes the epidural space.

The absence of a positive screening-trial result with the epidural method does not mean the intrathecal method would not have been positive. In a randomized clinical trial, Kalso et al² showed that morphine delivered through continuous epidural infusion gives the same analgesic results as morphine delivered via continuous subcutaneous infusion.

In 101 randomly assigned patients, 51 were implanted, resulting in many IDDS-related serious adverse events (Table 2¹). In fact, in 21 patients, catheter revision was necessary, and in nine patients, pump revision was necessary. These maneuvers cause patients pain and distress; moreover, pump revision requires an additional abdominal incision. This result is not stressed in the discussion.

With regard to the statistical aspects of the paper, we also found problems. The first sentence of the "Statistical Analysis" section states that "all eligible patients with required data at baseline were included in the analysis," but in the "Results" section, we find that in 101 IDDS patients and in 99 CMM patients, only 73 and 75 patients, respectively, provided data at the 4th week of follow-up, and only 72 and 71 patients, respectively, are considered in the pain reduction analysis (Table 3¹); no reason is given for this discrepancy. What about the intention to analyze all patients with baseline data, as stated above?

Because the primary measure of clinical effectiveness (pain reduction at the 4th week) gave no statistically significant evidence of difference between the two groups (P = .055; last column, Table 3¹), the study outcome was redefined, or, better, multiply redefined (Table 4¹), but the results only reached the minimal .05 significance level. Despite this, in the text, the authors use the words "significantly superior" to describe the results reported in the table. This is an example of a misuse of P values to overestimate borderline results; the results could have been presented more correctly and in a clinically relevant fashion, showing 95% confidence intervals (CIs) of the difference in response between the two groups. Considering the data from the table, we calculated the 95% CIs to be from 0.2% to 27.2% for the 13.7% difference of the first line of Table 4, and from -24.6% to -0.03% for the -12.3% difference of the third line. As can be seen, the intervals contain values different from 0% (which means no difference between the treatments) but close to 0% (0.2% and even -0.03%).

A different analysis was then presented: the "as treated analysis," the results of which seem to be stronger (that is, in favor of IDDS treatment). The authors hypothesize that this could be because many IDDS randomly assigned patients actually were not treated with IDDS; if this were true, why perform the efficacy test after randomization? Why was it not performed before, with the positive results added to the efficacy test as an inclusion criterion (and thereby reducing the target population to those who were actually eligible for IDDS treatment)?

Moreover, the survival difference in the two different groups was supported by weak evidence of statistical significance (P = .06, log-rank test) but was, in the comments, dealt with as if it were much stronger.

Furthermore, the last statistical analysis, which aimed to evaluate the association between the drug toxicity score reduction and survival, stated, ". . . improved mortality in the IDDS group may be partially explained by effects of the intrathecal pain therapy," and was inappropriate. Even if such an analysis were conducted with more suitable statistical techniques (such as time-dependent covariates in a Cox model—a technique not mentioned in the paper),³ the association between drug toxicity score reduction and survival cannot be considered an effect of the treatment; this effect could simply be because patients with drug toxicity score reduction are patients with better baseline characteristics that were not taken into account in the model specification.

In conclusion, multiplicity adjustments would have been necessary given the high number of tests performed.

We believe that this is the report of a study in which the results are borderline and statistical methodology has been used to present them as stronger than they actually are.

Considering the weak results given in favor of IDDS and the high number of adverse events, we wonder, in clinical practice, how often intrathecal catheter implant could give extra value with respect to adequate medical personalized treatments in a continuing-care setting.

REFERENCES

1. Smith TJ, Staats PS, Deer T, et al: Randomized clinical trial of an implantable drug delivery system compared with comprehensive medical management for refractory cancer pain: Impact on pain, drug-related toxicity, and survival. J Clin Oncol 20:4040–4049, 2002[Abstract/Free Full Text]

2. Kalso E, Heiskanen T, Rantio M, et al: Epidural and subcutaneous morphine in the management of cancer pain: A double-blind cross-over study. Pain 67:443–449, 1996[CrossRef][Medline]

3. Marubini E, Valsecchi MG: Analysing Survival Data From Clinical Trials and Observational Studies. Chichester, UK, John Wiley and Sons, 1995

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