One of the most difficult questions a scientist must resolve is which problem to investigate. An especially critical aspect of this process is getting the timing right. When you start working on a new problem, it always takes time to get the experimental system working. Then you have to get your data, write it up, and publish. By this point, years can have gone by, and what was cutting edge when you started may have become passé.

The converse can also be true. If you are addressing a novel question in a new field of research, you can certainly avoid the danger of being scooped by your competitors. However, you face the more significant risk of being ignored. If a scientist publishes a paper in an empty field, does it make a sound?

Historically, the scientific community has tended to ignore science that is too innovative or ahead of its time. For this, we are often accused of being biased towards maintaining some fictional status quo. The reason these papers often get forgotten, however, has more to do with the usability of innovative ideas, rather than some perverseness. The classic case is Gregor Mendel, whose pioneering ideas on inheritance were ignored for many years. It wasn’t because the scientific community did not know about him; Mendel simply addressed different questions than other scientists at the time. Years later, when chromosomes were identified as a potential mechanism for transmitting genetic information, his ideas suddenly became relevant to a much wider scientific audience.

In the 1980s, I published a number of mostly ignored papers on how to combine mathematical modeling with experiments to understand cellular responses to growth factors. Today, this approach is central to systems biology, but at the time, building computer models of cells was seen as a specialized, esoteric area of research. Why? Mostly because the technologies that could validate these models were extremely limited, and so could only address small-scale problems such as bacterial chemotaxis or receptor endocytosis, not big questions, like I suggested. It took advancements in molecular biology, large-scale genomics, and analytical technologies to provide the types of systems-wide data needed to make computational models more generally useful.

At the time, it was also hard to accept the thought that my research ideas were too innovative to be funded. All my proposals to NIH on computational modeling went down in flames. However, I have since come to realize that grant review panels are only interested in problems that they want solved. Unless I can convince them that a set of proposed studies will address current scientific problems directly (i.e., have “high impact”), they are unlikely to indulge my request for funding—and rightly so.

Most graduate students and postdocs seem to appreciate this concept, for I have observed a strong desire among young scientists to receive plaudits from their mentors and fellow students for the trendiness of their research project, and for how current it is. Unfortunately, this usually leads them to fields and research projects that are popular, resulting in intense competition for publishing original research findings and obtaining jobs and research positions. Although my use of computer modeling did not have the scientific (or funding) impact that I desired, it separated me from the pack of people looking at the trendy questions of the day, and certainly did help me get a job. Innovative investigators are highly sought after for faculty positions because they tend to make the most interesting colleagues.

So what to do? In some respects, you are damned if you do and damned if you don’t with respect to being innovative. However, I came to realize that you are penalized far less for using innovative approaches to solve current problems than for working on an innovative problem that is too far ahead of its time. To identify current problems that are just a little ahead of the field, talk to colleagues and go to small scientific conferences.

Nevertheless, I still reserve some of my research time to study problems of personal interest. It might take years before the rest of the community cares, but I am not doing it for the community. There is something ultimately satisfying about being the first person to explore a new area of research. Even if there is no one around to applaud.

Steven Wiley is a Pacific Northwest National Laboratory Fellow and director of PNNL’s Biomolecular Systems Initiative.

My experience and recollections concerning Wiley's lament over missed research opportunities, and science disregarded only to be embraced later, resonate well with his. Some respondents argue here that real scientists should get over it - we work at what we do without expectation of recognition. But some of us work at science for the value our conjectures, experiments, assays, and publications might have for humankind. And some of us grieve over lost support of some of our best work.
Over 30 years ago I submitted a grant application for support of an extension of my infant behavior research program which was well regarded and adequately funded until then. I wanted to do a study capitalizing on our by-then secure knowledge that newborn babies are capable of learning, and that infants go through a critical period around 2-4 months which is especially important neuropsychologically for survival. I had a hypothesis wanting testing that infants' learning processes (and learning insufficiencies), particularly during a period characterized by rapid myelination and dendrite proliferation, could be connected with sudden infant death syndrome (SIDS). The application was shot down, although the ideas had been presented with positive feedback at SIDS conferences attended by seasoned researchers and NIH science administrators.
Briefly (but see my paper, "Crib death: A Biobehavioral Phenomenon?" Current Directions in Psychological Science, 2003, 12, 164-170 for history and explication - electronic copy available), babies may succumb because of a behavioral deficit resulting from an inadequate transition from subcortical/reflexive to cortical execution of defenses against respiratory occlusion. Testing the hypothesis is feasible without further jeopardizing vulnerable infants' wellbeing. Nonetheless, the study was refused.
Of interest is that the NIH/NICHD did accept the supposition that respiratory blockage is involved in SIDS, and instituted formal cautionary instructions to parents and hospitals (and now day care centers) that babies should be placed for sleeping on their backs and not prone. I am, of course, pleased that a behavioral intervention has been accepted as a guard against crib death. While the incidence of SIDS has been halved since implementation of this warning, however, NICHD still has not issued a call for research proposals which might connect SIDS specifically to critical learning processes.

Lewis P. Lipsitt, Ph.D.
Brown University
Lewis_Lipsitt@Brown.edu

My experience in 30 years of basic and applied research, with many pushes of the envelope, leads me to the conclusion that, far too high a proportion of reviewers or potential sponsors are either too risk-averse to be occupying the positions they hold (approving only safe bets re their own reward schedule) or too risk-prone to discriminate between well developed and superficial, but flashy, proposals. Between the two, we seem to be wasting a large proportion of the available resources - not the least of which are promising young scientists whose futures rest on the outcome of a quasi-random process.

Probably not. Great talker/writer, but poor doer.

As someone stated before here, Steven Wiley always tends to give a very good description of reality in science, which is good, but he also tends to support current practices. Given that these are clearly far from optimal, this is not good. To young scientists or others not yet fully established (i.e. having no permanent job) it may indeed be wise to follow Steven Wileyﾴs advice, but at the same time this makes sure that nothing will ever change.

Thank you, Dr. Wiley, for putting "the obvious" into understandable terms (or should I say "almost bearable terms" for those scientists whose careers are ruined, or nearly ruined, because their ideas are ahead of the times?). And thank you for putting it also into personal terms. Unfortunately, some creative scientists simply don't have the luxury of being able to work on their funded project and a side project also. And some young scientists, not yet tenured, are just too darned stubborn to waste their time on projects of incremental value instead of projects that could really expand our knowledge -- until it's too late and the tenure decision is a thumbs-down because of "lack of productivity."

I've come to realize that the current funding system -- specifically, the beholdenness of funding decisions to "peer reviewers" -- is not in the long-term best interest of science and discovery in this country. I tried personally to make a difference in this regard back when I had the opportunity (as a program director for a non-NIH Federal funding agency) but alas my sphere of influence was too small to make the kind of impact that needs to be made. Now that I'm retired, I read truly exciting, paradigm-shifting stuff in Science mag articles from European laboratories that validates ideas presented many years earlier by small-lab US scientists who were unable to get funded despite my best efforts. And I get really sad, not just for the individual scientists who were unable to develop those ideas but for US science, which is being overtaken in quality and relevance by our foreign competitors who are not held back by that holy-of-holies called "peer review."

I have to say, probably >80% of the scientists I've worked for or with (or know, or read about) do it to boost their ego above all else. Maybe not to the Craig Venter level, but still.

A strong sense of course of scientific research really helps. Ultimately all scientific research is application oriented. We, scientists do not work in vacuum, we do not work just to boost our egos or to fulfill the hidden desire to get ultimate recognition.
Rather, science has been a tool to understand laws of nature, to get to know and develop means for better and healthy living. It may entail understanding different phenomena and later finding technique to be able to modify them. Thus comes the relevance of scientific research. No questioning, the timing is everything.

- Dr. Vinod Nikhra
www.vinodnikhra.com

I especially hate Steve's last article about quitters sometimes win. It is not helping at all!

Steve,
generally speaking I tend to dislike every single one of your columns because you seem to me to always have the most politically correct, pro-stablishment of the opinions, but there is something no one can deny: you get reality right, weather we like it (reality) or not. I shall say thanks...

My experience was quite similar. In the mid-1980's the p53 protein was considered an odd cancer protein because if its gene were introduced into a normal cell (read immortalized tissue culture cell line)it did not cause the cells to be immortalized. My lab found that the protein responded to stress in the form of DNA damage, and suggested that p53 might have a role in normal cellular growth. The paper was initially rejected, along with a number of grant proposals, on the grounds that there was no evidence that p53 played any role in human cancer. The founding editor of a prestigious journal (with a four letter name) went so far as to suggest these observations were only of interest to a small circle of people. Flash forward five years- it was accepted that the p53 gene is mutated in the majority of human cancers, and p53 was Science's "molecule of the year". I don't think my timing was off, so much as the times changed. It was recognized that cancer can be caused by loss of function in growth control genes. While, this might seem obvious now, that wasn't the case 25 years ago. I would recommend anyone who is interested in how "paradigm change" influences scientific research read "The Structure of Scientific Revolution" by Thomas Kuhn.

# Do what you like to do and do what you believe in, do not bother about recognition or timing #


Thanks Venkata. An outstanding, as well as inspiring, piece of advice.

Good piece.The issue is not recognition, but the desire to inquire and find out Truth.For such passionate souls, recognition does not matter.Take,Socrates,Plato,Aristotle,Da Vinci.They persisted in what they were doing because they were interested in doing what they wanted and not for recognition.Best piece of advice to researchers is; Do what you like to do and do what you believe in, do not bother about recognition or timing.None can stop the idea whose time has come.

But indeed, this is the question. Do you, a scientist, want to be "so far ahead that no one can see you"? No, you don't. It's such a pain. But you should want it.

Elsewhere in this issue, the demise of taxonomy is mourned. We need to fund "outliers," both people who are ahead of their time and those who are behind their time (i.e. sustaining knowledge already gained). Only in this way can we maintain the full richness of science. By defending running with the crowd, you favor the madness of crowds over individual perspective, the whims of the reviewer over the creativity and insight of the individual. One of the great frustrations of our profession is that we can, with one sentence in a review, stymie an entire research program, while to gain support for a new idea takes months to carefully craft the perfect proposal, get it past the knives of the reviewers, and hope we're close enough to the interests of a program manager to avoid an ax at the end. It's a wonder anything new happens when sales and politicking must intervene between insight and action.