Cancer research: Playing it safe versus taking risks

If there’s one thing that cancer researchers, indeed most biomedical researchers in the U.S., know today it’s that the research funding climate sucks right now. Indeed, after the completion of the near-doubling of the NIH budget in 2003, during which time it was flying high, the NIH budget in essence crash landed–hard. Paylines, which had been well over the 20th percentile (meaning that over 20% of grant applications in any give deadline cycle were funded) plummeted to near single-digit ranges almost overnight. Indeed, I almost fell victim to this myself in 2004. The initial score on my R01 clearly fell into the fundable range at the time it was reviewed. Indeed, my SRO told me that I probably didn’t need to resubmit, which is something SROs, who are notoriously cautious and tight-lipped about such prognostications, just don’t do unless it’s a sure thing. Then there was a budget standoff in the fall, and all rewards were put on hold. Meanwhile, paylines plummeted. My grant ended up going from a sure thing, to my sweating it out wondering whether the new paylines would still leave my grant funded. I ended up being funded, but only just barely, as paylines plunged five points in a single year–an unprecedented single-year drop, or so I was told.

The reason I started out with this story is to highlight a problem that arises when grant funding becomes tight. It’s a problem that was highlighted in, of all places, this week’s TIME Magazine in story entitled He Won His Battle With Cancer. The “he” in the title is Lance Armstrong, whom we’ve discussed before in the context of his appearing with Jenny McCarthy hosting a celebrity poker match to support autism quackery. However, his support of autism quackery and energy drinks making questionable claims aside, Lance Armstrong does do some good things for cancer research, and he is without a doubt one of the best examples of someone who owes his life to scientific medicine and cancer research and who is frustrated at the seemingly slow pace of cancer research:

For an increasing number of cancer activists, researchers and patients, there is too much death and too much waiting for new drugs and therapies. They want a greater sense of urgency, a new approach that emphasizes translational research over basic research–turning knowledge into therapies and getting them to patients pronto. The problem is, that’s not the way our sclerotic research paradigm–principally administered by the National Institutes of Health and the National Cancer Institute (NIH/NCI)–is set up. “The fact that we jump up and down when cancer deaths go from 562,000 to 561,000, that’s ridiculous. That’s not enough,” says Lance Armstrong, 36, the cyclist and cancer survivor turned activist through his Lance Armstrong Foundation (LAF).

This conflict between basic science, which emphasizes the gradual accumulation of knowledge and understanding about the basic mechanisms by which disease–in this case, cancer–develops, and translational research designed to take that knowledge and translate it into actual treatments, is not a new thing. It’s a tension that goes to the very heart of the role of a physician-scientist that I’ve written about before. It’s also at the heart of the cultural divide that often exists between physicians and basic scientists. Physicians, seeing patients every day suffering from cancer, tend to be impatient and want results now, just like their patients, while basic scientists tend to emphasize understanding the basic mechanisms by which cells become cancerous, believing that such understanding is a prerequisite to developing effective treatments. These days, the balance is shifting back towards translational research:

A new and more radical approach is being taken by groups like the newly formed Stand Up to Cancer (SU2C), which plans to finance research designed to deliver big leaps and home runs rather than the incremental improvements that are more typical of mainstream science. The new focus for funding grants, said Dr. Eric Winer, chief scientific adviser to the Susan G. Komen Breast Cancer Foundation, in a conference address, is results: “What we want to see is research that is going to change the number of women that are diagnosed with, or more importantly, die of, breast cancer within the foreseeable future.” Others, like the Multiple Myeloma Research Foundation (MMRF), are trying a no-nonsense business model to speed drug development.

Doctors and scientists understand the frustration and the fear, and they don’t necessarily mind the nudge. “We do need to change. Something needs to be done differently,” says Tyler Jacks, director of the David H. Koch Institute for Integrative Cancer Research at MIT. “We have a lot of new insight, and we need to have a whole new collection of drugs, a new armamentarium.”

This sounds good in principle, but, as they say, the devil is in the details. The biggest problem is that, without a steady flow of basic science discoveries in the pipeline, translational research has no foundation upon which to build treatments and new drugs. Shifting research too far to the translational side may pay sort-term dividends, but at the risk of choking off the flow of new molecular mechanisms and targets upon which translational researchers depend. On the other hand, emphasizing all basic science without a robust translational component risks building up an embarrassment of riches with regards to understanding but no clear benefit to cancer patients. The basic science purist would argue that scientific knowledge in and of itself is a laudable goal in and of itself, and so it is. However, government-funded cancer research is a political issue as well, and cancer patients and advocacy groups expect to see concrete results for the money, and the very purpose of cancer research is to develop more effective treatments.

There’s another problem, however, with putting too explicit a translational requirement on research. I experienced this problem firsthand earlier this year the first time I reviewed grants for the Susan G. Komen Foundation, which emphasizes its “important new focus on speeding the translation of research discoveries to reduce breast cancer mortality and/or incidence within the next decade,” as described by Dr. Winer. Time and time again, I evaluated grants that I thought to be highly meritorious on the basis of science alone, but I had to ding them because they were too weighted to basic science and thus highly unlikely to result in any treatment that would have impact on breast cancer incidence or mortality within a decade.

To illustrate my point, it’s instructive to look at the history of one of the most commonly targeted oncogenes in breast cancer, Her2/neu. It was 1981 when Robert Weinberg isolated the neu oncogene from rats, which was later found to be the rat homolog of the Her2/neu oncogene in humans. The gene was cloned in 1985, and it was not until 1988 that Dennis Slamon discovered that Her2/neu is amplified in 15-30% of human breast cancers and is a poor prognostic factor, then 1990 before a humanized antibody to the gene produced. It then wasn’t until 1998 when Herceptin, the antibody against Her2/neu, was approved by the FDA for use in Her2/neu-positive metastatic breast cancer. In other words, it took 17 years from the discovery of the neu oncogene and 10 years from its identification as a poor prognostic factor in breast cancer until a treatment based on it was actually made available to patients with breast cancer, and it was years after that before it made a dent in survival rates for women with breast cancer. As you can see, translating molecular findings to actual treatments that benefit patients with cancer can take a long time, even under the best of circumstances and targeting the clearest of molecular targets. It may not always take 17 years, but it often takes at least a decade. In the case of Judah Folkman and antiangiogenic therapy, it took nearly 30 years from his idea that tumor angiogenesis could be a therapeutic target for breast cancer to the actual clinical trials of therapies based on his idea.

This recent movement towards more translational (i.e., practical) research could be viewed to be in part a backlash against the inherent conservative nature of the NIH:

The long-standing criticism, though, is that NIH/NCI is necessarily structured for caution, for limited returns based on individual scientists grinding it out in their labs–the three-yards-and-a-cloud-of-dust mentality. To get funding, individual researchers typically have to write grant proposals that demonstrate a reasonable expectation of success. “You have to have already done some of the stuff and then propose it, before they’re going to believe it’s the right thing to do,” says Dr. Ray DuBois, executive vice president of M.D. Anderson Cancer Center and a cancer researcher. A proposal can take months to write, so a rejection means the loss of a scientist’s productivity as well.

It’s even worse than that, of course, when times get tight. Not only do proposals take months to write, but it becomes increasingly uncommon for proposals to be funded on the first submission, thus necessitating even more difficult second and third submissions, each of which take as long or longer to write. Reviewers, acutely aware that money is tight, do not want to waste it. In addition, if a reviewer has eight to ten grants to review before a study section, he or she will realize that, at most, only one is likely to be funded? Which one should the reviewer advocate for? Finally, while it’s pretty easy to distinguish a grant in the top 20% in terms of scientific merit, it gets increasingly difficult to differentiate between, say, the 15th percentile and the 10th percentile or, even harder, between the 10th and 5th percentile. At that level, the grants are all excellent, and deciding which one is more “meritorious” comes increasingly down to more subjective factors.

There are other costs, as well:

There are opportunity costs to this system. Collaboration suffers as scientists guard their work to keep the money coming. Because the funding process favors experienced grant writers, young investigators can lose out. Such friction and lack of funds, some argue, are causing a brain drain to Singapore and other regions that are actively seeking to develop their biotech industries. “The incentives are totally misaligned. The repetitive nature of funding the same universities and the same people–all of these things add up to the stagnant position that we’re in,” says Doug Ulman, president of the LAF and chairman of the Director’s Consumer Liaison Group at NCI.

When government funding flags, others step in, in this case Stand Up 2 Cancer (SU2C). The approach is this:

It’s what happens next that is different. SU2C will not distribute funds to research institutions. Instead, it will assemble dream teams of scientists across disciplines and institutions, and they will work collaboratively on projects designed to deliver a product of sorts–as opposed to an academic paper–within a defined time period. Says Ziskin: “They can only get funded if they can produce a treatment.”

To vet and choose the projects, SU2C has recruited a high-powered scientific advisory committee chaired by Phillip Sharp, a Nobel Prize–winning cancer researcher at MIT. The selected projects will then be monitored by the American Association for Cancer Research. “What I hope to do is identify areas where we could accelerate progress, particularly in areas where there’s need–ovarian, pancreatic, glioblastoma,” says Sharp.

Additionally, 20% of the funds raised will go to higher-risk projects with potentially greater paybacks. It’s a science version of throwing it long. “If you run the same play every time, you’re not going to win the game,” says Armstrong. One of SU2C’s advisers was the late Judah Folkman, a famed cancer scientist whose pathbreaking theory that tumors grow via angiogenesis (creating their own blood supply) was resisted for decades. “There may be other Judah Folkmans out there,” says Ziskin. “We don’t want them wandering around for 40 years.”

This is an admirable goal. There’s little doubt that more funding to higher risk projects would be desirable, but it’s also fraught with peril. High risk research is by its very definition much more likely to fizzle and produce nothing. If an organization doesn’t realign its expectations to that knowledge, funding such projects risks producing an impression of even less progress than the present paradigm of incremental, “safe” research does. I’m also more than a bit skeptical of how a new paradigm that, instead of being designed to produce knowledge and publications, emphasizes producing concrete, measurable goals will necessarily result in more progress towards cures of various cancers. After all, how is this different from what big pharma does? Big pharma emphasizes achievable, concrete milestones towards new drugs or treatments. It has to. Its profits depend upon new products being developed. Indeed, it has been pointed out that SU2C is very much influenced by big pharma, including GlaxoSmithKline and Amgen.

More interesting is the concept of enforced collaboration. There’s little doubt that multidisciplinary collaboration bringing multiple viewpoints to bear on a problem has the potential to jumpstart progress, but the keyword is “potential.” Whether that potential will be realized is not clear. Moreover, who will lead such huge multi-institutional consortiums of researchers and thus be principal investigators on such grants? It sure isn’t going to be junior researchers or even mid-career researchers. It’s going to be the very same senior researchers whose hegemony and monopolization of research dollars are frequently railed against by the very people who champion such ideas. How this is going to “shake things up” in cancer research I fail to see. I also fail to see how this will be all that much different than the situation now, in which the biggest, best-funded labs, the ones whose PIs can forge these multi-institutional research alliances, will get richer. One other consideration is that this sort of research effort to some extent undervalues what would be the biggest bang for the buck, namely using the knowledge that we know now to reduce the risk of cancer and to make screening programs that can decrease cancer mortality available to as many people as possible. This latter effort is not as sexy as new high-tech consortiums of high-powered investigators working as multidisciplinary teams, because, workman-like, it involves the application knowledge that we’ve had for years, if not decades, to the population at large.

Still, my skepticism aside, I do think that more chances need to be taken, and there need to be funding mechanisms in place to support taking more chances. The NIH definitely rewards caution and punishes innovation, its claims otherwise notwithstanding The problem is finding the balance that results in the most efficient translation of basic science into effective cancer treatments. Unfortunately, lately, in this effort, I sense a denigration of the difficult, painstaking research that goes into characterizing the molecular mechanisms that need to be characterized before researchers can design these new bang-up therapies and a glorification of seemingly “risky” (translation: “sexy”) newer approaches. Whether that glorification is justified remains to be seen. In the meantime, I welcome attempts to shake up the current research funding paradigm. I just don’t share the faith that the new boss will necessarily be any different than the old boss.