Joan Roughgarden wanted to right what she saw as a long-standing wrong. Stephen Mojzsis wanted to find data that everyone assumed did not exist. Adam Riess wanted to answer some of our most fundamental questions: How old is the universe? How did it start? What is its fate?
Some scientists are driven to ask big, bold questions. They are committed to following the path to the answers even though it may lead to rejection, ridicule, personal attacks, lost funding, or other trials. They challenge prevailing assumptions, transform their fields, and experience the notoriety, both good and bad, that comes with being a game changer. Their audacity is not without cost. And sometimes they're wrong.
The cliché has been around for a long time: If you want to do important work, you have to pick an important problem. Like many clichés that endure, there's truth to this one. Roughgarden, Mojzsis, and Riess, whose stories we'll explore in detail in this series, have all been labeled "audacious"--a label that describes their choice of problems and their chutzpah in challenging the status quo. Riess and Mojzsis have cracked open rich new areas for research that will be explored for years and careers to come, although some of their ideas are still debated. Roughgarden's most recent work has found few supporters and remains highly controversial, though she insists that negative reviews of her work are slowing. It can be difficult to tell, contemporaneously, whose science will and won't endure.
What leads these scientists to do the work they do? Riess, an astrophysicist at Johns Hopkins University (JHU) in Baltimore, Maryland, didn't set out to discover dark energy or that the expansion of the universe was speeding up. He did it because it was fun to delve into such fundamental questions, he says.
Mojzsis, a geochemist at the University of Colorado, Boulder, didn't expect to demonstrate that life may have existed on Earth long before anyone thought it was plausible. He merely noticed that some key assumptions were based on "zero data" and decided that it would be "fun, and maybe risk-worthy, to see what I could find if I dug a little bit."
Roughgarden, a biologist at Stanford University in Palo Alto, California, had no intention of challenging one of Darwin's fundamental tenets of evolution. But, she says, when she discovered that the exceptions to Darwin's sexual selection theory started to outnumber the examples that fit it, she felt she had no choice but to take action. The science was just plain wrong, so Darwin's theory should be abandoned and replaced with a more inclusive social-selection theory, she argues. Although Roughgarden is widely respected and her competence is questioned by few of her colleagues, most reject her latest insights. Some critics insist her social views cloud her scientific judgment--a charge she reportedly rejects. But even if the charge is true, it doesn't necessarily make the science wrong.
None of these scientists woke up one day and decided to challenge the status quo. They followed their interests and their instincts--and other influences--where they led. And they led into the bold, edgy regions of their fields.
Let's assume that you wish to follow in their footsteps. How do you do it? How does one venture into these bold regions? Are there road signs declaring, "Big Discoveries Ahead"? Is audacity an essential character trait for paradigm-changing scientists? Can you just decide to do game-changing work?
And once committed to doing audacious science, how do researchers--especially young, early-career scientists--sustain their commitments in the face of the myriad aspects of the system (including funding, publishing, and tenure) --that seem stacked against risky endeavors? If pretenure scientists refuse to take scientific risks, science will be impoverished. But do we have a right to ask those young scientists to also risk their careers? Or should we encourage them to store away their boldest ideas until after they earn tenure?
These are some of the questions that will be explored in this series. But first, some groundwork.
It takes all kinds of scientists to move science forward. Not all pursue risky, paradigm-changing ideas--or should. Many of the scientists interviewed for this series insisted that their discoveries were made possible by frameworks laid down by the careful, incremental advances of their peers.
Everyone has a style of their own, says Steven McKnight, a biochemist at the University of Texas Southwestern Medical Center at Dallas, and incremental and risky styles of science are equally valid.
"If every advance was a major innovation, science would be an incomprehensible mess," says David Montgomery, a geomorphologist at the University of Washington, Seattle, and a 2008 MacArthur Fellow. "You can't base a broadly held body of knowledge on something that's growing by leaps and bounds every day. It just wouldn't work. Nobody could keep up." Incremental advances set the stage for the next major revolution in thought, he adds.
Roughgarden draws a fundamental distinction between "risky ideas that are extensional and bold ideas that are destabilizing." Most scientists, she says, believe that good science is built on the science of the past, which is assumed to be good science because it has passed peer review and is supported by consensus. "Scientists are often willing to take risks provided that the risk is in behalf of an endeavor or project that will extend what's already believed to be true."
"The problem is when you think that the consensus is wrong," Roughgarden says, and when your new proposals are "destabilizing to what's commonly believed." Then, she says, you're likely to hit a rough patch in your career. Roughgarden thinks that young scientists should do such work only if they feel they have no other choice, "if you just have to do it as a matter of conviction."
Yet conviction isn't the sole motivator of audacious science. Several of the scientists interviewed admitted that they simply were not cut out to do extensional, incremental science; they bored too easily, they said, which suggests a certain proclivity toward scientific risk. And scientists with that proclivity often don't stop at one game-changing idea; many are serial paradigm-shifters. Roughgarden's first controversy was over her work on the rocky intertidal zone in California--an experience that prepared her for what she calls "the kind of crap I'm going through now." Mojzsis is now on his fourth assault against prevailing assumptions about conditions on early Earth.
"When I say 'audacity,' I put two things together: original thinking and the willingness to go after whatever you are thinking about and not worry about what someone else will think," says JHU neuroscience legend Solomon Snyder.
A master decipherer of neurotransmitters, Snyder knows a thing or two about audacity. He is one of the world's most-cited scientists, was the youngest full professor in Hopkins's history, and, through a long and fecund career, has taken us deep into understanding the way the brain sends messages. He is credited with the discovery of opioid receptors and endogenous peptides, and he uncovered the role of nitric oxide and other gases as neurotransmitters.
"Boldness is the single most important thing in science, assuming you have basic talent and intellect and creativity," says Vilayanur Ramachandran, a behavioral neurologist and director of the Center for Brain and Cognition at the University of California, San Diego, who is known for designing simple, elegant experiments that offer profound insight into behavioral neurology. Richard Dawkins has called him "a latter-day Marco Polo, journeying the Silk Road of science to strange and exotic Cathays of the mind." Ramachandran says that it also takes a certain personality to make the discoveries that revolutionize a field. "You have to have supreme confidence," he says.
If audacity is the foundation for groundbreaking science, persistence is a key companion trait. "Persistence works in conjunction with risk-taking as the ability to have confidence in a vision of how things work and to test it," says Mark Fitzsimmons, associate director of the MacArthur Fellows Program at the John D. and Catherine T. MacArthur Foundation in Chicago, Illinois. The program awards no-strings-attached grants of $500,000 over 5 years--often colloquially called "genius grants"--to individuals from all fields, not just science, who "are making the big leaps, the big contributions, or will be," he says.
Intelligence is another integral component of audacious science, but it might play only a supporting role. "Having a high IQ and getting all A’s is not actually relevant at all," Snyder says. Students with these qualities "may do very well, but they tend not to be the ones who go on to greatness." Snyder recalls an evening hosted by his friend Tom Clancy, the novelist, and attended by "some very famous generals" to discuss success in the military. The people who rise to the top in the military don't necessarily get perfect grades, he observed, but they do get into trouble. Not jail-worthy trouble, but rebellious, nonconformist trouble. "Ultimately, ... you want guys like that, who think outside the box and who are sort of ornery, because they're the ones who do great things," Snyder says. "And you see that time and again in science."
Creativity is important as well, but a definition of creativity can be elusive. "One of the themes that I've always seen is that great scientists have in their family history or their own history a flair for the arts," Snyder says. "Being analytical and critical is important as a baseline. But if you focus too much on being critical, you never discover anything."
"When you see seemingly disparate ideas connected in a way that makes sense and coheres, that is an indication of a kind of creativity that we look to support," says Fitzsimmons.
"So creativity is key. But that alone isn't enough because lots of people have lots of great ideas," Snyder says. "And what matters is doing something about them. If you're timid, you don't do anything. So that's where audacity comes in."
"Among all scientists maybe one or two or three in 10 are the kind who just don't want to do what is obvious. They want to take a leap into the unknown," says McKnight, who studies the role of proteins in switching genes on and off. He discovered the genes that control the body's internal clock, telling it when to eat, sleep, and wake. He received one of the National Institutes of Health's nine inaugural NIH Director's Pioneer Awards in 2004.
McKnight compares science to the Lewis and Clark expedition. "Ninety-nine percent of what they did was slog. It was brutally hard. You barely made it, and then you step over and see a valley that no one has ever seen before. Then it's spectacular." The adventure of science is an endless frontier, he says. "Nothing's cooler."
McKnight says that intrepid scientists must be willing to take risks. "The biggest fame comes to the person who makes the discovery that no one else was even thinking about," he says. "And that's the willingness of a young person to just venture into the unknown."
"It's more important to do 10 high-risk experiments, nine of which fail completely. But the one that's succeeded is of earthshaking importance," Ramachandran says.
But how many young scientists can afford to fail completely nine times out of 10?
"If you want to ensure professional security, it's hard to be bold and take on enormous risk because you just might fail, and if you fail, you only get one shot as a young, untenured professor," McKnight says. In addition, the conventional wisdom--which many of the scientists interviewed for this story say is true--is that review panels for major grants from agencies such as NIH and the National Science Foundation are risk-averse. Roughgarden hasn't gotten funding for her research in years.
One way of managing the risk, suggest many of the scientists interviewed, is to borrow a concept from the investment community and apply an asset-allocation scheme to your portfolio of research projects. "The solution is to do something boring and derivative--dotting the i's, crossing the t's--and get your grants on that basis but at the same time, in parallel, pursue the bold projects," Ramachandran says, "because nobody said you can only do one thing at a time." Other ways to pursue risky science will be discussed later in this series.
Scientific audacity is not so much about being brash and pushy, Snyder says. It's about being fearless in following research where it leads without worrying about potential consequences such as renewing grants and securing tenure. That's easy for him to say: He founded JHU's neuroscience department, which is now named after him, and has been renewing the same R01 grant since 1966, the year he was appointed to JHU's faculty. That's evidence that bold science, at least in the best cases, can lead to a long and fulfilling career.
Coming up in Part 2: "Taking the First Steps Toward Audacious Science"
Anne Sasso is a freelance writer and may be reached at amsasso at nasw dot org.