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Research Locally, Think Globally

Focusing on details may get you published, but what do we lose in the process?

By | July 1, 2008

I participate in several grant review panels each year that cover different areas of biological research. Despite the relatively broad subject areas that they address, such as signal transduction or genomics, I have noticed a strong similarity between many of the proposals I see. They tend to be focused on a few, relatively narrow topics that have been studied for years, and use just a handful of approaches. For example, in the field of signal transduction, it is common to see proposals to investigate the epidermal growth factor receptor (EGFR), but rare to see a study on other types of receptors. Yet the EGFR is the receptor type that we know the most about. A PubMed search on EGFR yields more than 10,000 papers. Repeating the same search for the insulin-like growth factor receptor, however, yields less than 150. There are many other examples.

In short, biological knowledge, like these proposals, is concentrated in a few areas separated by large swaths of ignorance.

There are many different reasons why. Some of this stems from a few schools churning out a disproportionate number of scientists in a particular field. Anyone know the story of Yale graduates and their influence on cell biology research? George Palade, a Nobel Prize winner, started a graduate program in cell biology at Yale in the early 1970s. This program generated more than 100 PhDs mostly focused on intracellular organelle biogenesis, which thus became a dominant theme in the field.

Technology is also a prominent reason for the heterogeneity of biological knowledge, because a new technology can tell us a lot about specific processes while leaving others obscure. For example, antiphosphotyrosine antibodies have allowed us to easily follow tyrosine kinase signaling pathways, but downstream signaling events mediated by other activated enzymes remain a mystery.

There are ways to bridge these gaps. Take new technologies, for example. MicroRNAs, which were discovered using genomics technologies, could fill many holes in our knowledge of mechanisms of posttranscriptional gene regulation and signal transduction. I do have a fear, however, that microRNAs will also become a specialized field, as has happened so many times before. Why? Because biologists are typically reductionists, who tend to pursue a general observation down to its most fundamental level.

Reductionism is driven by basic human nature and our difficulty in comprehending complex processes. Reductionism in biology is also strongly driven by journal reviewers. I can't count the number of times that I have submitted a paper only to have some reviewer ask for more details, extra experiments, and clarification of some arcane mechanism that was irrelevant. Eventually, reviewer expectations become our own when we have the opportunity to review our colleagues' papers. However, it is not realistic to expect that details will eventually add up to comprehensive knowledge. Biological systems are simply too complex, and we will end up knowing a lot about trees and being clueless about the forest.

Focusing on details might help get your papers published, but it is not the best approach to getting your grants funded. Reviewers, myself included, tend to be more impressed by the novelty or the broader impact of a proposal rather than its ability to exhaustively explore a problem. This does not mean that scientists should be superficial in their investigations, but that we should be more aggressive at filling in the gaps between our work and that of others.

There are a number of ways to do this. Make sure you are aware of the latest technology, because it can move your research in new directions. Take advantage of online citation resources. Who is citing the major labs in your field? If other fields are finding connections to your area, you are likely to find connections to theirs. But the most important thing is to simply try something new. Systems such as the EGFR are most important as models, rather than ends into themselves. Take the approaches that have proven successful in model systems and apply them to something different. It might be difficult at first, but you are more likely to discover something new. And isn't that why we became scientists in the first place?

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

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Comments

July 14, 2008

As senior PhD students and early career post-docs slowly morph into tenure track investigators, the issues that this article addresses are important and fundamental. It is very easy to go with the flow and often times the reasons of doing this are not clear. \nThe matter of filling gaps where research information is thinly spread or non-existent is of particular relevance when one thinks of scientists in developing countries.
Avatar of: Beverly Barton

Beverly Barton

Posts: 7

July 16, 2008

The real question to ask is when will NIH fund truly innovative projects? That is why you see research clustered in a few areas.
Avatar of: Claudia Gabaglia

Claudia Gabaglia

Posts: 1

July 16, 2008

NIH reviewers do not like risk takers, nor bridge proposals linking different fields. The "too ambitious", "focus in 1 Aim" and "lack of preliminary data" are very common comments for grants with broader approaches, especially from "young" investigators who are most likely to think more globally, as the author recommends.
Avatar of: anonymous poster

anonymous poster

Posts: 7

July 16, 2008

The author of this article makes the following observation about the grant proposals that he has reviewed in the past: "They tend to be focused on a few, relatively narrow topics that have been studied for years, and use just a handful of approaches. For example, in the field of signal transduction, it is common to see proposals to investigate the epidermal growth factor receptor (EGFR), but rare to see a study on other types of receptors. Yet the EGFR is the receptor type that we know the most about."\n\nHe assumes, based upon this observation, that researchers are not being innovative/creative, not willing to use new technologies/approaches, and/or not willing to move out of their own comfort zones to examine new, unexamined areas or areas of broader significance. However, he fails to address a separate, yet related problem: most of those researchers writing grants have had at least one reviewer that blackballs their novel, innovative, and significant proposal because it is risky. For example, a researcher I know personally wrote an NIH proposal focusing on a poorly-studied angiogenic factor, only to have it rejected, based upon (in part) a reviewer comment that she should focus on VEGF, a very well-studied angiogenic factor, instead. This is only one example of an innovative, novel proposal with a negative outcome. It is comments and outcomes like these that force researchers to propose relatively safe, less significant, and less innovative projects. \n\nIn my experience, many, if not most, researchers have innovative, creative, novel ideas, but feel that the only proposals that are funded are those that are safe and virtually guaranteed to work. The problem does not lie with the researchers, but rather with reviewers and an overall system that do not appear to value creativity and innovation.
Avatar of: Bradley Andresen

Bradley Andresen

Posts: 34

July 16, 2008

The article is, in my opinion, very well written and hits the nail on the head, but then so do many of the other comments. I am a young scientist (4 years as faculty, 1 as tenure track), and I have many times been told that my proposals are to ambitious. Additionally, the work I do studies smooth muscle cells in the kidney, which I have shown do not signal the same as the typically used thoracic aortic smooth muscle cells. I bring this up because I also get slapped with the lack of innovation because I am trying to determine the signaling properties, and I describe experiments that will test known pathways from other cells. Without a reference it is very hard to define a pathway in a new cell, but because I use a reference I am not innovative! I have to side with the other comments that clearly state our review system is broken. If you can predict the outcome of a grant is it really worth a 5 year 250k/year R01?
Avatar of: anonymous poster

anonymous poster

Posts: 5

July 16, 2008

Fund more female researchers. Studies have indicated that female scientists see the complexity of systems and design their research to answer big picture questions. While some programs have attempted to fund based on a female gender preference they have used a male-dominated review panel using the same small window of approval and therefore the programs have been less than successful.
Avatar of: anonymous poster

anonymous poster

Posts: 9

July 16, 2008

What's your point? We don't have innovation nor truly diverse areas of research. NIH with no money has to show accountability and fund the "sure things". I am sure a lot of the grumbling would tend to disappear if more money was freed up for grant funding. \n\nReviewers seem to like only techniques they use or can understand. Or--they ask that applicants consider the technique du jour, and penalize you if you don't. What we also need is a wiser and diverse pool of reviewers. From my experience, every grant I submit is a crapshoot--we should put the objectivity back in and eliminate the subjective reviews that emanate from an unevenly qualified/experienced reviewer pool. \n\n\n\n

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