Taking chances

My laboratory is trying to make transgenic mosquitoes. We hope to find out if it is possible to decrease the transmission of infectious agents (such as those that cause malaria, which world-wide kills one person every 20 seconds) by altering the disease vector so that it is no longer a suitable host. There are some indications that this approach could be successful. Dengue-virus-resistant mosquitoes have been made at Colorado State University using an antisense system (which is unfortunately not heritable). We’ve been working on transforming mosquitoes for over five years. What keeps us going, and what are the consequences of taking on such a risky project? In an intellectual and scientific sense, our project is no riskier than many other efforts. But principal investigators, postdoctoral fellows and graduate students need to produce results within timescales relevant to grants and job offers. Although I know we’ll develop a transformation system some day, I can’t say exactly when. So I, and the people in my lab, face a career risk due to current views on how public money should be spent. Edward Lewis spent his whole life working on the genetics of segment determination in Drosophila, and got a Nobel prize for it. Nowadays, that work would probably be considered too risky to fund. The problem with setting out on a research effort that may be long-term, has few publishable interim milestones and is difficult to fund is that the scientific community recognizes and rewards success, not the accumulation of knowledge that precedes success. Some research groups develop creative strategies for publishing incremental advances, but their reviewers soon lose patience. The expectation of a ‘publication gap’ when you start a risky project has different effects on lab heads, postdoctoral fellows, and graduate students. A five-year project is well beyond the scope of an aggressive postdoc, but is just within reach of a good graduate student. Is this a fiveyear project or not? The uncertainty frustrates everyone. You can see the disillusionment set in. The effect on graduate students is particularly brutal. They start out eager to work on an important problem, swayed by the nobility of the cause and the enthusiasm of the lab head. The lucky break is just around the corner. But if it doesn't happen in time, they are left scrambling for publications. For lab heads with tenure, the immediate career effect is not so devastating. All we have to worry about is lab morale, the competition for funds, and the fact that we’re forced to admit publicly and often repeatedly that the latest experiment, yet again, has failed. A friend recently admitted that he used to think that the problem with mosquito transformation was the incompetence of workers in the area; he now knows better, but many of my colleagues must secretly feel the same. Given all this, what motivates someone to undertake a risky project? All I can say is that the work is important and it needs to get done. This leaves me with the uncomfortable feeling that ‘risky science’ as a whole depends on the quixotic whims and energy of a few individuals. If so, then there is an additional risk to science in that, one day, there may be no one eager or able to take up the challenge. Some hopeful changes have recently reduced the risks a little. Grant-giving bodies are becoming more aware of the need to fund long-term research, and private foundations (in our case the John D. and Catherine T. MacArthur Foundation) have been particularly responsive. The MacArthur Network on the Biology of Disease Vectors has now formulated an action plan (see http://klab.agsci.colostate.edu/mfnet/ mfnet.html) to make it easier both to reach the final goal and to share credit for success among all the groups who contributed to it. Career and ego damage may be even more important than funding problems, however. A while ago, the NIH initiated a program to fund “high-risk, high-impact” science. Remarkably, no one that I know of in the mosquito community applied. As money gets tighter, fewer people are willing to take any risks at all. The funding changes and networking arrangements also don’t help postdocs and graduate students with their need to show productivity in the short term. I know of no good solution to this problem. Many lab heads try to give each student a lowrisk project to work on in parallel with the risky experiments. But risky science demands a lot of attention and the low-risk projects often get put off. And succeeding at such a project isn’t enough to elevate creative, hard-working risk-takers above their risk-averse peers. True, people in the field know what you’ve done, but this doesn’t help when a postdoc or graduate student applies for a job. Strong recommendations from lab heads have their limits. Science offers one the thrill (described by Lewis Carroll) of trying to hold two contradictory facts in your mind at once. As the projects that need doing become increasingly difficult, we have to address the contradictions in our attitude towards risky projects. We urgently need to find a scientific solution to the problem of rewarding those who are willing to take risks on our behalf.