Usually, when I curl up in my favorite wingback armchair by the fireplace to read the latest issue of Journal of Clinical Oncology or Blood, a brandy snifter on the mahogany side table, the bowl of my pipe filled to the brim with my favorite brand of Old Hickory tobacco, and my trusted Labrador retriever, “King,” curled by my feet, I rush straight to the “Statistics in Oncology” section of the journal to complete my vision of the perfect evening at home.
Okay, there's a lot wrong with that scenario. I don't think I own anything fancy enough to be called an armchair; brandy makes me retch, as does smoking; I don't own a dog (though, if I did, I would probably name him “King” in homage to the old Rodney Dangerfield sketch, in which he claims, “When I'm at home, my wife treats me like a king, calling out to me, ‘Here, King! Here, King!’”); and any section of a journal that involves statistics is often a valid substitute for Ambien to help with sleep.
But one recent article published in June in JCO (2011;29:2439-2442) did catch my eye, because it deals with an inherent challenge in requiring overall survival as the ultimate, gold standard endpoint to randomized trials in oncology. In it, the authors (Korn, Freidlin, and Abrams), all from the National Cancer Institute, play out different scenarios of how difficult it is to conduct a study of an experimental therapy vs. a standard therapy with a clean survival endpoint.
How can survival be anything but straightforward? You're either dead or alive, right?
Well, yes, but how you get there can be murky. Most trials start out cleanly enough. A patient with metastatic cancer is randomized to either experimental, or standard, therapy. The patient remains on that therapy until progression or death or unacceptable toxicities. The problem lies in what happens to that patient if she then goes on to get another therapy.
Let's say that the experimental therapy (B) controls the cancer better than the standard therapy (A)—seems as if the experimental therapy eventually should provide a survival advantage to the patient over standard therapy. But what if, upon progression on either study arm, the patient goes on to get a different, standard therapy (C) that works better at controlling the cancer after standard therapy (A) than it does after experimental therapy (B)? Any survival advantage to the experimental therapy (B) will be eliminated, and if the study has as a primary objective to detect survival differences between study arms, it will be a negative study.
Okay, but what if the subsequent standard therapy (C) works just as well at controlling the cancer in both arms. You should then be able to see that survival advantage that the experimental therapy (B) provides, right?
Maybe, but you might miss it. Remember, studies are powered to detect percent survival differences. Let's say that, with experimental therapy (B), a cancer patient lives 12 months, but with standard therapy (A) she lives 9 months. That's a 33% improvement in survival—rock on! But, what if subsequent standard therapy (C) extends patients' survival on both arms by three months. Now, the survival advantage to patients on the experimental arm (B) compared with those on the standard arm (A) is 15 months vs. 12 months—still a three-month difference, but now only a 25% improvement for the experimental arm (B)—which may not be significant if patient sample size is not increased. Again, we may be left with a negative study.
Allowing crossover to experimental therapy in a clinical trial is VERY appealing to patients who have run out of standard options (or for whom standard options don't work), and to those of us consenting patients to clinical trials; but this makes determining a survival advantage to an experimental therapy a real morass.
If the experimental agent works great in the first-line metastatic setting, but not so good in second-line (when those patients initially randomized to standard therapy (A) could cross over to experimental therapy (B)), it shouldn't make much of a dent in the survival advantage it provides to first-line patients on experimental arm (B), and we could still have a positive study. But if the experimental therapy (B) works only pretty well in the first-line setting, and a little less well in second-line, we will again be left with a negative study.
All this theoretical study design talk makes my head hurt. I think I'll take that brandy now.
But these are real issues we face many times a year when we discuss drug applications at the Oncologic Drugs Advisory Committee (ODAC) at the FDA. How do we distinguish a true lack of survival advantage to an experimental drug that is just simply not very effective at controlling cancer, from a statistical lack of survival advantage due to a watering-down of a real treatment effect, because of subsequent standard or even experimental therapies?
It's not easy. Recognizing that, to paraphrase a common saying, “subsequent therapies happen,” and desperate patients are very good at seeking out other treatments when the one they are taking fails (I know I sure would be), randomized controlled trials powered on determining a survival difference for an experimental therapy should take this into account in determining the sample size needed to show a survival difference at the design stage.
Crossover should be avoided whenever possible, but particularly in cases when crossover is allowed because of an interim analysis based on an intermediate endpoint that may not be a surrogate for overall survival.
And remember, if an experimental therapy works really, really well at controlling, or even eliminating cancer, what happens subsequently doesn't make that much of a difference. It's only because many of these therapies aren't as effective as we need them to be that we have to read statistics sections in oncology journals, thereby ruining a perfectly good evening by the fire.