I offer, for the edification of my readers, a few thoughts I've had about cancer research, garnered from 3-plus decades in the lab and the clinic. I cannot claim originality, as some of these are flat out steals, and I suspect the rest probably have been thought of by others. But I offer them in the hope that they may be of some interest.
1. Ideas are cheap. Work is hard.
I worked with Larry Einhorn for a good part of my adult life. Early on, whenever I would go somewhere to give a talk, one of my hosts would claim that he (my host) had originated the idea of using platinum-based therapy for testicular cancer, and it was only by chance that Larry had gotten there first with his PVB regimen. Later on, I met an engineer who claimed to have come up with the idea for the personal computer before Jobs and Woz, only to be stymied by his corporate bosses. I would add that, whenever I have had a brilliant idea, I have only to open a scientific journal to find it in print. Ideas are cheap, and frequently "in the air"—at least in retrospect and in popular memory—but work is hard. PVB and
Apple were the result of a dose of luck, and some smarts, but mostly lots of hard work done at the right time.
2. It's OK to sleep with a hypothesis, but you should never marry one.
This one was shared with me by an astute, if crude, laboratory researcher; it has been attributed to Sir Peter Medawar, the Nobel laureate immunologist. We sometimes think it heroic to battle for a scientific hypothesis that everyone else disagrees with. I call this the "They said Thomas Edison was crazy" phenomenon. But my experience with the few great researchers I have known is that they are thoroughly unsentimental about their hypotheses. They try out one after another, test them as rapidly as possible, and move on if they are wrong. And even when they are right, the great ones are serious pruners, clipping off the unneeded and the extraneous until the truth is revealed in all its glory. A wise variant of this maxim comes from Darwin's bulldog, Thomas Huxley: "Another beautiful hypothesis murdered by a nasty, brutish fact."
3. A good drug makes everyone look smart.
A decade ago, melanoma doctors were considered lower life forms by breast cancer doctors. Now breast cancer doctors have serious melanoma envy. Melanoma doctors have not gotten smarter, nor have breast cancer researchers voluntarily undergone frontal lobotomies. Checkpoint inhibitors and vemurafenib came along, serving as chemoattractants for the fresh talent flooding the field. New England Journal of Medicine papers started popping up every 2 weeks. Lots of great science, too, but a good drug makes everyone look smart.
4. No one is smarter than a phase III trial.
A few years ago, I was chair of the ECOG Breast Cancer Committee. We had just completed E2103, our phase III metastatic breast cancer trial of anti-angiogenic therapy, with a doubling of progression-free survival in the metastatic setting. It being the height of the "wisdom of crowds" fad, I polled the committee, asking them to predict the results of our just-started adjuvant trial. Ninety-four percent of the attendees felt it would be a positive phase III trial. I was part of that crowd. With such an overwhelming vote, why even bother to conduct the study? Well, because…we were not as smart as a phase III trial. We seriously didn't have a clue.
The other common variant on this phenomenon occurs when the phase III trial is positive. Almost immediately, individuals start individualizing: altering doses and schedules, substituting drugs, changing duration of therapy. These alterations lead to either increased toxicity or decreased efficacy or both. Alternatively, we discount the results of the trial because it differs from our personal experience or biases. We think we are smarter than a phase III trial. Repeat after me: no one is smarter than a phase III trial.5.
5. Scientific papers are the first rough draft of scientific history.
With apologies to The Washington Post's Ben Bradlee, of Watergate fame, to whom the original version of this maxim is attributed, minus the "scientific." A great research finding is rarely the end of the story.
More often it is the middle, and sometimes only the beginning of a new trail of discovery, a jumping-off point. I have had numerous colleagues, most smarter than I am, who fell into "analysis paralysis," trying to create the perfect scientific paper, one for the ages. They usually get scooped by the guy writing "the first rough draft" of scientific history.
6. Quantity has a quality all of its own.
The scientific literature is mostly crud. This is true both in the lab and the clinic. Lack of reproducibility is endemic. One of the major reasons for this is the curse of small numbers: cell line experiments that use only one cell line (rather like treating a single patient and expecting to discover a universal truth), animal experiments with a few lonely mice, clinical trials with suspicious "descriptive" statistics. Small numbers studies are particularly prone to overcalling results, and we, lemming-like, follow them over the cliff in our ever-recurring credulity.
Last year, I heard a presentation where a new combination therapy was said to have an 89 percent response rate. Translated into English this meant that, in a preliminary, unaudited analysis, eight of nine patients had shown initial signs of response. The next time I heard the study presented (more patients, longer follow-up, external review of results) the response rate had dropped to 54 percent. Still respectable, but not the second coming of the Salk vaccine. Quantity has a quality all of its own.
7. Biology is destiny.
Having lived through over 3 decades of research, I have seen many promising therapies come and go. The ones that have stayed have almost always been biology-based. This was not obvious for the first half of my career, a period dominated by the pursuit of ever longer acronyms, ever-higher doses, and application of therapies based on "unmet medical need," a euphemism for "we can sell a lot of drugs for this bad cancer." Though "Toothpaste A + Toothpaste B" empiricism regularly rears its ugly head, the last 15 years have seen the long-overdue triumph of biology in cancer medicine. By the way, this isn't because we were stupid then and we are smart now. We have better tools, and hard-won knowledge. We're still quite capable of stupid.
8. Biology is messy.
If biology is destiny, that doesn't mean it is either easy or clean. Biology is gloriously messy. We regularly get confused. Like the drunk who uses the lamppost for support rather than illumination, we latch on to some biologic story, holding on for dear life, often long after the story is shown to be incomplete or even flat out wrong. Even with a "clean" drug like trastuzumab for HER2-positive breast cancer, we spend the good part of 2 decades arguing over exactly how it works. This doesn't bother me a bit. I love messy. We're cancer biologists, not physicists, after all. Not everything has a single, simple explanation. Remember Walt Whitman: "Do I contradict myself? Very well, then I contradict myself, I am large, I contain multitudes."
9. Knowledge isn't power.
I know, Francis Bacon is rolling over in his grave right now. But knowing isn't enough unless you know enough. We've known that KRAS is really important in pancreatic cancer for decades, and as far as I can tell it hasn't improved anyone's overall survival, because we haven't been able to shut KRAS down outside the laboratory. Knowledge, let me repeat, is not power: successful application of knowledge is power. Take BRAF in melanoma. Remember sorafenib? The drug that was going to change the face of metastatic melanoma? But vemurafenib isn't half bad (well, only 49% bad, since it doesn't work all that long, but who's counting?). Or PARP inhibition for breast and ovarian cancer: remember BiPar's iniparib, which wasn't really a PARP inhibitor? Bad tools won't test the hypothesis, but that doesn't mean the hypothesis is wrong. Another Bacon quote is preferable: "Nature to be commanded must be obeyed."
10. Nice drugs get beat up in bad neighborhoods.
I cannot tell you how many times, over the years, I went to a cooperative group meeting, or an advisory board, and heard a proposal to try a new drug in fifth-line therapy for this disease, or the same drug in that disease, where absolutely nothing ever works. In the former case, the usual explanation is that we have all of these (lousy, inadequate, toxic, borderline useless FDA-approved historical accidents of) drugs that we have to try first. In the latter case, "unmet medical need" is the excuse for hoping that a drug will magically transform a disease for no other reason than we want it to do so. Hope is not a strategy. Hard targets are hard for a reason. Nice drugs get beat up in bad neighborhoods.
I could go on, but 10 is a nice number, as Moses understood. And I've run out of fingers.