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.
We'll also see the rising importance of the wishes and beliefs of the big donors to these private funding entities.
I have to wonder how much interference a lab might face with growing interest/impatience of VIP donors.
And I wonder how universities are reacting to the implications of patent rights of the discoveries.
Good post.
This
is of great importance, but takes us beyond the realm of funding priorities and into politics and social struggles.
The NIH definitely rewards caution and punishes innovation, its claims otherwise notwithstanding
Wrong. It is the study sections that reward caution and punish innovation, not the NIH. I yearn for the day that the NIH tells its overcautious, I-fund-me-and-my-friends, sure-this-is-how-the-SRA-tells-us-to-score-it-but-we're-just-going-to-do-what-we've-always-done-anyway study sections to pack up and go home.
In the current setup for peer review at the NIH, from the perspective of investigators submitting grant applications that's a distinction without a difference.
I have to disagree. The study sections control the NIH's behavior. If we (the scientists who make up the study sections) want the behavior of the NIH to change, we have the power to make that happen. That we choose not to makes it our fault, not the NIH's fault. It's fun to scapegoat the NIH though for the conservativeness of grant review.
I'm coming at this from a bit of a different perspective. As an engineer, I've spent much of my career influenced by Deming's work on industrial quality. What I get from this is the need to apply science to the process of research itself.
I mean, come on! We have decades of raw material to work with now. It should be possible to put together a model (subject to refinement, of course) of the research process from the clueless freshman to established treatment.
Because it will be (necessarily) a statistical model, the optimal interventions at each part of the process will also be "fuzzy." I'm sure that you'll just love having your funding depend on a literal toss of the dice, but then again I'm not so sure that's much worse than what you're up against today.
Very thoughtful post. I'm in basic science, and I'm very concerned with studies and findings that I can relate to the clinic, but I know many people in my field consider clinical relevance to be a very distant second behind their basic findings. NIH of course requires clinical relevance, but I think they could be a lot more stringent about it. And perhaps the basic scientists need to be galvanized or otherwise convinced to really puch work that could move into the clinic, though other than requiring it for funding, I'm not sure how you could do it.
This kind of brings home the need for these particular studies. What is the recommendation to folks as they keep running into things like this?
"We have decades of raw material to work with now. It should be possible to put together a model (subject to refinement, of course) of the research process from the clueless freshman to established treatment."
That has not been overlooked by the companies that invest billions in drug research. There are "streamlined" processes in place that are meant to optimize results but... there's still a large probabilistic component that cannot be controlled. It's even harder as scientific discoveries shift the research environment.
That's the problem. Once a field advances past a certain point, you can't know a priori which lines of inquiry will turn out to be essential to future progress. My favorite example is number theory: mathematicians went forever smugly content that it would never have any practical application and then some schmuck discovered that you couldn't do real cryptography without it and the world's financial traffic needed cryptography. Ka-BOOM: number theory is suddenly a required course for a bunch of smelly, grubby-handed computer science types. Bummer.
Looking at the stuff in my field (semiconductors) that's hitting the market now, and then working backwards to the basic research, you find that when the basic research was being done there was no anticipation at all that it would end up being a gating factor on hundreds of billions of dollars a year in business.
They funded the research (mostly in materials) because, frankly, there was a degree of faith that materials research pays off. Not that much faith involved, really, since most of the technological advances of the last 200-plus years were in large part gated by the availabilty of necessary materials. It's a good bet.
Unfortunately, for whatever reason, we don't have that degree of "faith" in basic biological research. Partly, perhaps, due to the relatively short time that clinically-useful results have stemmed from basic science instead of purely pragmatic trial-and-error. We should recall that less than three medical careers ago, the germ theory of disease was still controversial. (Cue John Scudamore.)
... "optimization" depends very much on your desired objectives, and for all of the TFH-resistance in the world it's no secret that pharmaceutical companies' idea of "optimum" isn't necessarily one that the rest of us would agree on.
Notably, a steady slow trickle of improvements that are actually exploitable for 20 years each is perfect from where their stockholders stand.
@scicurious: I'm doing translational research and even when I hit study section in the face about the impact my work would have on cancer patients (I design novel anti-cancer therapeutics), funding is a long-shot. The need to reproduce (not produce, big difference) preliminary data before a study section smiles on me is daunting.
When I read the following, a chill went down my spine:
People in my field have been dealing with the "multidisciplinary mandate" of NSF grants for years. It's become sort of a mantra with funding agencies of late - the idea that getting people from different disciplines and different intitutions together can spark some sort of "magic" that leads to groundbreaking research.
In my view, this is the result of faulty hindsight. Yes, some major breakthroughs have come from research groups that were either multidisciplinary, multi-site or both. However, that doesn't mean that putting together a "dream team" of people from different fields will produce anything other than chaos.
I've had a few good multidisciplinary cooperative projects, and all of them have been with people I had met well before the "team" was assembled. We all knew each other beforehand and decided, often after years of informal discussions, to work together on a specific project.
I've also been on a few projects that were "multidisciplinary" because the funding agency gave priority to "multidisciplinary" projects (with funding the way it is today, we'd wear pink tutus if that gave us an additional 5% chance of being funded). The best of these projects was difficult, frustrating and didn't live up to its promises. The worst of them led to a prolonged lawsuit between two of the universities involved. None of them was as productive as the individual members of the group would have been if they simply worked on their own.
This fascination with "multidisciplinary" groups is beginning to fade - at least in the basic sciences, where I work. To be sure, the NSF still talks up "multidisciplinary" research, but it doesn't seem to get as much of an advantage as it once did. I suspect it will run the same course in NIH funding and - if it happens - in funding from private organizations.
The other issue with a "dream team" is that the "top people" in any given field are not always the easiest to work with (e.g. Craig Venter). They often do very well as the Lord High Principle Investigator and very poorly as a collaborator. Running a "dream team" might be a lot like herding cats.
As a (relatively) young researcher, I'd like to see less emphasis placed on "track record" but, as a taxpayer, I like to see my tax money spent wisely. The sad fact is that my proposals don't get funded as often as the "big names" because I'm perceived to be a bigger "risk". The "big names" have shown their ability to do research and get results - that's how they got to be "big names". I don't like it, but I can understand why the NIH and NSF do it that way.
It would be interesting to see the advocacy groups actually funding research instead of just lobbying Congress to increase research funding (with our tax dollars). If they would fund more "risky" ventures, that would be a good thing. If they want to "bridge the gap" between basic science knowledge and the pharmaceutical companies, that would also be a good thing.
With luck, the groups like SU2C will get past the business-school rhetoric and learn how good research - even good translational research - is done and fund people who are interested in doing it.
Prometheus
The famous observation by Arthur C. Clarke seems to apply. The gray eminences in any field are usually very good people to have running incremental improvement research and very poor people to have doing basic research. (And, yes, I deliberately used two different verbs.)
Good post. This is exactly the mindset that leads down the path to woo. If you make your time horizon short enough and only accept proposals that (claim they) can have an impact during that time horizon, then only proposals that (claim they can) be successful in that time frame can be considered.
Orac, against stage 11 cancer (that is cancer that has progressed beyond stage 10), your SBM is useless. Only a "miracle" can be successful, so only proposals promising miracles can be funded.
DC, that is exactly the problem. Thomas Kuhn pointed that out too, scientific peers are good for doing what he called "ordinary science". Which is science built on the paradigms that the peers are working with. When those paradigms are wrong, the peers can't see it. Anything that is inconsistent with the scientific paradigms of the day is by definition high risk, even if it is correct.
Says Ziskin: "They can only get funded if they can produce a treatment."
Isn't that what pharmaceutical companies do when they sell treatments? By selling the treatment they have produced they get funding. If research is only funded after it has produced a treatment, then it will never be funded because it can never be done. If you know how to do something before you do it, it isn't called research.
I think another quote from Arthur C. Clarke fits too. "Any sufficiently advanced technology is indistinguishable from magic". If the reviewers can understand it, it isn't "sufficiently advanced" and so won't produce the "magical" results that are required.
"It would be interesting to see the advocacy groups actually funding research instead of just lobbying Congress to increase research funding (with our tax dollars)."
I like that idea!
Would you comment on the book "The End of Medicine"?
What do they mean by "produce a treatment", a drug which works in cultured cells? Tumour bearing mice? Early clinical trials? It will always take a long time to convert basic science to an actual therapy as there are some steps that can not be shortened. These include toxicity testing, determining how the drug is optimally absorbed, and actual clinical trials on patients, where you need a couple of years follow up data at least to convince yourself that the drug is doing something.
We lose a huge amount of potential drugs simply because of solubility, absorption and side effect issues (this has significantly affected small molecule inhibitors of angiogenesis). No amount of "risky" research on out-of-the-square targets will make these issues go away. An innovative drug aimed at a previously unthought-of target will still have to grind its way through pharmacokinetic trials and toxicity trials before we give it to humans.
And of course, if your conceptually new drug (or therapy of any sort) is tested in the wrong animal model (because you haven't done the basic research to work out appropriate models in the first place), then you can lose your drug that way (this is what happened to paclitaxel [Taxol(r)], it had to wait a significant amount of time until appropriate cancer models were developed that could detect taxol's effect).
For a view of the cancer drug search from a drug development point of view, and an insight as to why "great leap forward" approaches are unlikely to succeed, see this post at "in the Pipeline".
In the case of angiogenesis, converting the knowledge that angiogenesis is critical for tumour growth into effective treatment has taken nearly 20 years, in part because of a need to understand the basic science (which angiogenesis factors? at which stage in tumourogenesis? are mutants important? how do you avoid mechanism-dependent side effects?).
As this 2008 review states, However, the results from clinical trials have not shown the antitumor effects which were expected following preclinical studies. It appears that clinical applications of antiangiogenic therapy are more complex than originally thought.. You will not get effective translational research until your basic research ducks are lined up properly.
Giving Judah Folkman container loads of cash in 1980 would not have significantly sped up the deliver of antiangiogenic drugs to the cancer clinic (although interferon alpha has been used since 1988 to successfully treat hemangiomatosis and angioblastomas, extension to other tumour types has been a long, hard road).
DC Sessions: "... "optimization" depends very much on your desired objectives, and for all of the TFH-resistance in the world it's no secret that pharmaceutical companies' idea of "optimum" isn't necessarily one that the rest of us would agree on.
Notably, a steady slow trickle of improvements that are actually exploitable for 20 years each is perfect from where their stockholders stand."
Oh, give me a break. Pharmaceutical companies want the new, big-break revolutionary blockbuster as much as anyone else. Multidisciplinary project teams and screening systems are organized to burn through new target ideas as fast as possible to scout new areas and toss out unlikely prospects. The trouble, as Ian Musgrave correctly identifies, is that most of this work is simply tough and requires a lot of basic research. In cancer drug discovery there are pitifully few validated targets. Most targets chosen for screening have mere whispers (often just a small handful of published reports) of possible influence in cancer.
One thing I could add to Ian's comments is that the effectiveness of most prospective anti-cancer drugs isn't known until they go into clinical trials. Animal and in vivo model systems translate poorly (They're better than nothing but the failure rate for cancer drugs in the clinic remains steep). And yet, for some cancers there are so many drugs going through trials that it can be hard finding enough patients for all each clinic study.
Nice post, dude. Here's a few clarifications:
(1) Your explanation of a payline is incorrect. It is not the percent of grants that get funded. Rather, it is the percentile of priority score within which grants are funded.
(2) It is not a Scientific Review Officer who would be discussing the score of your grant with you. It is a Program Officer.
(3) Resubmissions never take as long to prepare as initial submissions.
Newsweek also has an interesting article on cancer research this week. It goes more in-depth than the Time article about trends and challenges in cancer research, and addresses prevention at the end.