It's Not Just About Innovation

Last year, I was a reviewer of proposals to a newly created NIH program, the New Innovator Award. Its goal was to address a frequent criticism – that peer review is biased against innovation – and to fund exceptionally innovative, high–impact research from new investigators. To encourage the submission of innovative ideas, the agency didn't require preliminary data. We received nearly 2,200 applications, but awarded only 30, for a success rate of <1.4%. This suggests either that there are many unfunded innovative ideas out there, or that the ability to submit a proposal without preliminary data was irresistible.

Our mandate was to evaluate the importance of the proposed problems, the innovativeness of the approaches, and the investigator qualifications. Almost all the problems were important, and many approaches seemed quite innovative; however, ranking the degree of innovation was difficult. Was developing a microfluidics device to automatically measure Caenorhabditis elegans more innovative than customizing nanoparticles for photothermal tumor therapy? So, despite not requiring preliminary data, we ended up awarding projects mostly from accomplished young investigators who demonstrated they had done some groundwork and knew the idea could work. (See the New Innovator Award Recipients to make your own evaluation of the winners.)

Expecting reviewers to rank these grants based on their degree of innovation was probably a vain hope, in any case. Assessments of innovation are purely subjective; what is commonplace for one scientist will be extremely novel to another. Building a computer model of cancer might be innovative to an oncologist, for example, but it could seem simplistic to a chemical engineer. Most breakthroughs in science take place not through the generation of entirely new ideas, but through the application of concepts from one field to another.

All reviewers like innovation and creativity in grant applications, if for no other reason that it makes them much more interesting to read. However, new ideas are only a starting point for an exciting research project; there must be a reasonable possibility that the new ideas will work and will have some impact. Obviously, the easiest way to convince a reviewer that your idea will work is to demonstrate it with much preliminary data. Many investigators take this tack, leading to grumblings that NIH will fund only studies that are mostly finished. This is not strictly true, for I have read successful proposals penned by gifted writers who can convince by words alone. (Full disclosure: I usually end up packing my grant applications with large volumes of preliminary data.)

When I was a young scientist, I thought that the insistence that I provide evidence of the practicality of my ideas was profoundly unfair. As I became older, I started appreciating review panels' points of view. Many of my wonderful ideas, in fact, did not work as planned. The reasons for failures were many, usually related to biological systems being much more complex than initially expected. Some were doomed because of conceptual flaws, such as not understanding system noise. Some were simple in concept, but extremely complex in implementation, such as building display libraries.

When good ideas hit a roadblock, one always needs to judge whether the effort will pay off. I have dropped many promising ideas because I simply did not have the time or commitment to make them work. After all, fresh new ideas that haven't been soured by reality are always more appealing than yesterday's idea that has become a pain in the butt.

Over the years, I have observed that very few innovative ideas are ever brought to the point where they have made a significant impact on biological research. Grant-review panels implicitly understand this unpleasant truth. The defining characteristic of successful ideas are bright and preserving scientists who believe in their ideas and are willing to do whatever it takes to make them succeed. What Thomas Edison said about genius is equally applicable to innovation; it, too, is mostly about perspiration.

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