Timing is Everything

By Steven Wiley Timing is Everything You want to be ahead of the curve, but not so far ahead that no one can see you. It was hard to accept the thought that my research ideas were too innovative to be funded. 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 al

Steven Wiley
Aug 1, 2009

Timing is Everything

You want to be ahead of the curve, but not so far ahead that no one can see you.

It was hard to accept the thought that my research ideas were too innovative to be funded.

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...

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.