Reply to Greg from Martin Chalfie

Dear Greg,

Your concern about the applicability of your research is important, but I feel that the pressures on all researchers (especially new researchers) may be different now than when I began my research career.  Many of my ideas about research were formed while interacting with colleagues during my postdoc beginning in 1977 at the MRC Laboratory of Molecular Biology in Cambridge, UK. All of us at the LMB were encouraged to do whatever experiments we wanted, but we were always asked why we chose the particular projects we did.  We always had to justify our experiments.

But the sense of the question was different then.  We were not asking about the applicability of the research to a particular disease or specific application; we wanted to know about the importance of the biological question that we were addressing.  For me and my colleagues who worked on the nematode Caenorhabditis elegans, this justification hinged on the belief that studying basic biological processes in a genetically tractable eukaryote, which could be studied with single cell resolution, would provide insights into biological problems in a wide range of organisms, including humans.

Thus, justifying one’s research and thinking about its consequences are crucial aspects of what we do as scientists, whether we are responding to nonscientists who want to know about our work, writing papers and grants, or pondering our results. We do not just do experiments and accrue data. These days, however, I believe that scientists feel more pressure to justify their research in terms of more immediate outcomes.

In recent years governmental officials, university administrators, and clinical researchers have called for a greater emphasis on ‘translational research’, research that translates findings in the laboratory into new treatments for medical conditions, over basic research. They want to see results that answer the questions of greatest importance to them, and they sometimes question funding basic, open-ended research.  Although the application of biological and biochemical research to human disease is important, I feel that the current increased emphasis is unnecessary and is actually detrimental.  The emphasis is unnecessary because most scientists are already strongly motivated to think about the implications of their work, and it is detrimental because it concentrates on assumed end results.

I am not against translational research (especially as I get older). I am, however, concerned that the current push for translational research does not allow for a balanced approach to basic and applied research in the biomedical sciences.  I was dismayed, for example, that when the National Institutes of Health (NIH) first used the ARRA stimulus money to fund 100 Challenge Grants, and 98 of them were in areas that appeared to be directed toward translational problems.

Part of my discomfort with the push for translational research (or any push for a specific outcome for scientific research) is that the usefulness of basic research is almost never obvious and often takes many years to develop. This aspect of our work is very hard to convey to nonscientists.  Few, if anyone, would have predicted the usefulness of lasers in the 1950s or of green fluorescent protein (GFP) when Osamu Shimomura discovered it in 1962.  As many people have said, translational research requires having something to translate, and that material is the information and insights provided by basic research.  If we narrowly focus research only on human diseases, we will, ironically, miss the information that may ultimately help us understand and treat human afflictions.  That belief in the importance of our research that I shared with colleagues in Cambridge has been confirmed many times over the subsequent years.  For example, studies on C. elegans identified genes that are essential for cell death (a process whose control is disrupted in cancer), discovered RNA interference and micro-RNAs (which are the bases of new means of controlling cell function and activity), and introduced GFP as a biological marker (which has allowed investigators to study a wide variety of human diseases in model organisms).  None of these breakthroughs came from research directed at answering specific disease-related questions, but all of them undoubtedly helped the study of diseases — as have the vast majority of research projects conducted in C. elegans and other organisms.

Nonetheless, the allure of translational research for the general public is very strong. People, especially those who themselves or whose family members are affected by a debilitating or life-threatening disease, want to see results. They do not understand the complexity of biological processes or how episodic our understanding of disease is.  Discovering a gene that is mutated in a human disease doesn’t cure that disease, but it can be the start of understanding. I sometimes feel that the lay public, perhaps because they are accustomed to hearing scientific success stories, has little understanding of how slow most scientific progress is.  The sequencing of the human genome did not produce cures for countless human genetic diseases within ten years, but it did provide insights that made those cures closer to being realized.

We need to participate in the education of the public, but at the same time strike a balance so that we explain our results without over-selling them. Part of this education process involves explaining to the public that basic research is not the selfish pursuit to satisfy intellectual curiosity. An important aspect of peer review is that the importance of all research, basic and applied, must be explained, and funding proposals have passed the rigorous test of providing appropriate and meaningful justification of the significance of the work.

You quoted Francis Collins in a New York Times article saying “We’re not the National Institutes of Basic Sciences. We’re the National Institutes of Health,” a statement that seems to imply that support for basic research is doomed.  In fairness the paragraph containing this quote started with an acknowledgement of the importance of basic research. Indeed, both basic research and applied research are needed. As I said above, I feel that encouraging a shift to translational research at the expense of basic research (sometimes with the misguided idea that scientists must have already learned enough) will not cure the world’s ills, and may have the perverse effect of discouraging the public’s faith in the scientific approach.

So what should a beginning scientist do? I side with your undergraduate advisor and say that you should start by picking an important biological problem.   This problem could be related to disease or not, but it should be something that will allow you to push the limits of our knowledge. And it should not be chosen because you think it is more fundable. While studying this problem, you should also try to interact with as many scientists (and clinicians) outside your area of expertise as possible and use their insights to address your scientific concerns and issues.  This interaction is where the real translational research occurs. As I said at the beginning of this letter, drawing inferences from our work is an important aspect of who we are as scientists. One of the intellectual joys of research is being the first person to connect disparate ideas or results.  Having as many diverse inputs is essential for the discovery that makes science the exciting enterprise it is.

All the best,

Marty