You've decided that you're not interested in taking on science's smaller, safer, more manageable problems. You don't intend to be cautious or retiring. You won't settle for the fringes; you are bold, a risk taker, and ready to change the world.
"It's very easy to confuse the secondary reinforcers with the primary. Then you lose sight of your original goal to make amazing discoveries." --Vilayanur Ramachandran
Can a scientist just decide to do audacious science? It looks as though a person with a solid foundation and a good mind can, indeed, decide to become a bold scientist. Our conversations with, and the careers of, a few audacious scientists offer some rough guidelines. Scientific audacity starts with a passion for a topic. It requires the judicious selection of an institution and a mentor. And it necessitates searching for an important problem. Do these things and your chances of doing important science improve?
Follow your bliss
There are fields in science, and points in their history, that are especially fertile for radical change. But that doesn't mean you have to be in those fields or work during those auspicious moments. All the researchers we interviewed, from diverse fields including neuroscience, biology, geology, and astronomy, agreed that there were few scientific barriers to audacious thinking in their respective fields. The most important consideration in choosing a field, they say, is passion.
All these scientists have displayed passion in their own careers--evidence that passion increases your odds of doing paradigm-changing science. Yet this claim requires qualifications. First, although passion may be necessary, it certainly isn't sufficient. Not every passionate scientist does audacious science. And many audacious, passionate scientists end up being wrong.
The next qualification is that a passion for the field--or even for science--isn't always evident at the outset of a scientific career; it may begin as a spark of interest then deepen and mature into a defining, driving commitment.
Coming up: Part 3: Funding Audacious Science.
Early in their careers, young people may "just kind of follow their nose and do things that are interesting," says Sara Seager, a planetary scientist at the Massachusetts Institute of Technology in Cambridge. "And I think often this is a good thing." Seager began working on exoplanets--planets that orbit stars other than the sun--before there was any consensus about their existence. She wasn't even particularly committed to having a career in science. "I really had nothing to lose," she says.
In hindsight, that lack of commitment allowed her to take a really big risk early in her career: to study an emerging field. "At the time, there was just a handful of [exoplanets] known. And many people disputed their reality, because when you're looking at a planet around a star, in most cases you don't see the planet, you only see the effect on the star," she explains.
As her involvement with the field deepened, her commitment grew. She felt she was on the cusp of important discoveries. The people interviewing her for faculty positions, though, didn't share her conviction. Their skepticism was frustrating--even disheartening--but by then she was on a mission. "Once you get committed to something, you will probably have more insight than other people, and then you really just have to stick with it," she says. Her commitment paid off with a lot of firsts, including the first discovery of an exoplanet atmosphere.
Find a nurturing environment
To do bold science, you need a mentor with a commitment to pursuing big questions, preferably based at an institution with a long-range vision. "Some institutions, based on their leadership and their access to internal resources, can be more supportive of bold science than others just by virtue of whether they have their own money to spend on it," says Steven McKnight, a biochemist at the University of Texas Southwestern Medical Center at Dallas.
McKnight had both in his favor: a supportive institution and mentor. He started his career at the Baltimore, Maryland, branch of the Carnegie Institution of Washington, which had an endowment. There, he worked with Donald Brown, who "just wouldn't have anyone who wasn't trying to go for it and do something substantial," he says. "If I had been doing incremental, obvious science, he would have admonished me."
Later, McKnight set up his own lab with the aim of facilitating bold research. "Everyone knows, 'Don't go to Steve's lab unless you're crazy,' " he says, because his lab isn't a direct route to science's usual currency: publications, tenure, and funding. "As soon as some breakthrough is made and there become obvious things to do, I get tired of them. I'd rather have other people do it," he says.
"Every student or postdoc who works with me is doing something that may or may not work. And it may take them 3, 4, 5 years, and then it doesn't work and they have nothing to show for it," he says. "And maybe that's irresponsible on my part, but they come in and we start working on something and they're in the unknown."
Plenty of other scientists offer mentorship and succor to students unwilling to practice safe science. But because they are distinctly a minority, finding them may not be easy. McKnight suggests starting your search at institutions that, based on their leadership and access to internal funding, are supportive of bold science. He cites the Carnegie Institution of Washington, the Stowers Institute for Medical Research, and the Howard Hughes Medical Institute as incubators of boldness. Researchers supported by these facilities have "every opportunity in the world to take bigger risks," he says.
Vilayanur Ramachandran, a behavioral neurologist at the University of California, San Diego, advises students to seek the "masters" and avoid, "like the plague," people who have lost interest in what they are doing. Science has become professionalized, he says. "Consequently, that excitement that science is sort of a great romantic adventure gets eclipsed. And the student who enters the field has to say to themselves, 'Look, the whole point of this enterprise is not to get grants or not to get things published,' although that's important, of course, to get over the hump and make tenure and get money. But it's very easy to confuse the secondary reinforcers with the primary. Then you lose sight of your original goal to make amazing discoveries."
There appears to be a strong element of self-selection in the process of choosing mentors and institutions. Personalities that are bold will find a way to do what they want to do. Students who know themselves to be uncomfortable with risk will stay away from places like the McKnight lab. Students like Seager will find mentors who support their bold pursuits and, later, encourage their own students to take chances.
The support of Seager's postdoc mentor, the late John Bahcall of the Institute for Advanced Study in Princeton, New Jersey, was essential to her postdoctoral research on exoplanets even though it was not Bahcall's field of study. "He felt that if you had an idea that you could solidly argue for … and that sometime in the near future an observation could be made to support your theory, then he thought it was great," she says. Seager was already accustomed to going against the current, but knowing that Bahcall thought well of her and her work was very important, she says.
Joan Roughgarden, a biologist at Stanford University in Palo Alto, California, says, "When students have come to my lab, I've made it really clear that this is really risky stuff, and if you want to do it, you're getting in on the ground floor of a whole new approach to gender and sexuality in nature." If the students are "radical at heart," Roughgarden's lab is welcoming, she says. "If they're looking at how to get ahead, my lab isn't the place to come because they'll be identified, at least to begin with, with a minority position."
Choosing an important problem
Finding problems to work on doesn't seem to have been an obstacle for the scientists interviewed for this series. That's not surprising; after all, we selected them because they have already proved their ability not just to identify but also to make progress on important problems. But the choice of a problem can be daunting when you're just starting out. Some great scientists appear to be born with a knack for identifying the right question, Seager says. But even for them it takes a bit of searching.
"It's too much to ask--and too intimidating as a young person--to expect them to have enough grasp of the field to know where the rich veins will be," says Adam Riess, an astrophysicist at Johns Hopkins University in Baltimore. Seager believes that students can learn to identify interesting areas and ideas, but they need help at the beginning. There's not much alternative to relying on mentors.
Seager's focus on exoplanets goes back beyond the Bahcall postdoc to her Ph.D. adviser at Harvard University, Dimitar Sasselov, who offered her a range of research topics. She chose to investigate exoplanet atmospheres. "I learned from this person more from osmosis and by watching and trying to learn how to identify new ideas," she says. "It's something I was always trying to pay attention to."
One strategy is to avoid crowds. "If anything is hot and trendy and popular, stay away from it," McKnight says. "Pick a direction where you think there's potential, ripeness, where other people are not going, and just dig in and see what you get."
Ramachandran agrees. Humans are great mimics, and crowded areas of research develop a false aura of importance. Your grandmother may be a better judge of what's important than are your colleagues, he says. "Because they're all in the same cul-de-sac with you: they publish each others' papers, review each others' grants, review each others' papers in journals, so you get lulled into this feeling of doing something important." The excitement that surrounds hot topics at big scientific meetings can be especially pernicious, Ramachandran says.
It's important to avoid the seduction of following the crowd--to step back, look at the big picture, and ask big questions. "What is the question that is driving this? Why are they doing all this?" Ramachandran says. "Not, 'Are they doing it properly? Have they proved it well? Have they done all of the controls?' All of that is secondary. The first question is, 'Why are they doing it; is it important?' "
Another rich source of problems is a field's fundamental assumptions: Are they solid or merely the prevailing consensus? Stephen Mojzsis, a geochemist at the University of Colorado, Boulder, says that one of his scientific pet peeves is "assumptions based on zero data." He describes his start in his area of research: "The conundrum was that it appeared there was no [sedimentary] rock record from before around 3.8 billion years. And people threw up their hands"--assuming and asserting that surface processes during that period of Earth's history were unknowable. "And even if we could find out anything, it wouldn't be interesting because the Earth at that time was a molten, uninteresting slag heap."
So Mojzsis sought out samples of the oldest sedimentary rocks known, located in Greenland, and found a carbon signature suggesting that life may have been present when the sediments formed. This discovery, published in Nature in 1996 "opened up the possibility that biological information could be preserved even in the oldest sediments," he says. Today, Mojzsis continues to unravel the fascinating story locked in their structure, suggesting life on Earth far earlier than previously thought.
Following Mojzsis's example requires a solid foundation in your field's fundamentals, he says. Once that groundwork is established, anyone can challenge fundamental assumptions. "It becomes a mindset," Riess says. "You're constantly asking yourself, 'How do we really know that this is true?' And when you sense that there's a weakness in it, then that's where you probe."
Yet another way to uncover ideas with potential is to ask the right people. "Often, the ones who do come up with a lot of ideas don't have the time to work out all of the ideas for themselves," Seager says. "There's a nice thing about ideas: They're free," adds David Montgomery, a geomorphologist at the University of Washington, Seattle. "And people who are creative, I think, tend to keep them coming."
Image: (top): Artist's concept of the star Fomalhaut and the Jupiter-type exoplanet that the Hubble Space Telescope observed. A ring of debris appears to surround Fomalhaut as well. The planet, called Fomalhaut b, orbits the 200-million-year-old star every 872 years. Credit: ESA, NASA, and L. Calcada (ESO for STScI)
Anne Sasso is a freelance writer and may be reached at amsasso at nasw dot org.