How To Spur Scientific Revolution: Amass Copious Data, Keep It Simple

It's another late night in the lab, and you are poring over a data set that just doesn't make sense. No matter how you crunch the numbers, they just don't fit. Unless. . . . If you disregard the generally accepted model and ignore the ideology of the day, an intriguing mechanism emerges. Your midnight model explains all the data, but it runs counter to everything you've been taught about biology. You'd be in good company. In the past, scientists have grappled with some seemingly bizarre concepts: DNA that jumps around the genome; RNA that catalyzes a molecular reaction; proteins that may behave like genetic material. But they stood by their ideas, secured funds, and managed to amass enough evidence to win over even their most dubious critics-in some cases, receiving a Nobel Prize for their efforts. How did they manage to turn alternative theories into something mainstream? And what can you do to fuel your ideas with the power to overturn the paradigms of the times? Maybe you could take a tip from Thomas Kuhn-a science historian and philosopher who was at the University of California, Berkeley, when he published the definitive work on the evolution of scientific paradigms, The Structure of Scientific Revolutions (University of Chicago Press, 1962). According to Kuhn, who died this past June (Notebook, The Scientist, July 8, 1996, page 30), scientific progress follows a pattern: Scientists plod steadily along, amassing data like bricklayers building a wall, until a crisis precipitates a major intellectual upheaval and the dogma du jour crumbles. FROSTY RECEPTION: Agricultural scientist Bill Liebhardt met resistance to his idea for managing crop production. The breakpoint often rests on the accumulation of data that cannot be explained by the prevailing model. Before a crisis, scientists try to understand their problems within the context of current thinking, observes Bill Liebhardt, the director of the University of California's Sustainable Agriculture Research and Education Program in Davis. "If something doesn't fit the model, many scientists won't pursue it." Liebhardt has encountered more than his share of opposition to his sustainable production ideas-such as allowing cows to graze in pastures that are rotated from season to season rather than resorting to bovine growth hormone to enhance milk production. When he presented that rotational grazing idea at a meeting five years ago, Liebhardt says, it met with a frosty reception, even from dairy scientists. "There was a lot of resistance out there," he recalls. "Some people will go to their deathbed believing that [their] model is the correct one." INTELLECTUAL UPHEAVAL: David Stump notes that a lot of proof eventually leads to scientific revolution. But at some point, the data can no longer be overlooked. "In the Kuhnian version of a scientific revolution, all the little problems add up to the indictment that the popular theory is wrong and they're seen as the key to a new theory," explains David Stump, a professor of philosophy at the University of San Francisco who teaches Kuhn's theories. Of course, not just any upstart theory can displace the dominant dogma. "A discovery is only credible when several different approaches come up with the same conclusion," reports Marlene Belfort, a molecular biologist at the Wadsworth Center of the Department of Health in Albany, N.Y. Belfort discovered that prokaryotic genes may be divided by introns-intervening DNA sequences that scientists originally believed were unique to eukaryotes. "The more far-out the discovery, the more skeptical the scientific community will be, and the more rigorous the proof needs to be," she says. Take ribozymes, for example. When Thomas Cech at the University of Colorado in Boulder first suggested that certain RNA molecules could catalyze enzymatic reactions-a talent ascribed exclusively to proteins-researchers were dubious, Belfort says. "Until Cech could synthesize RNA and show that RNA alone had catalytic activity, he was always up against the protest that a protein contaminant in his sample provided the activity," she states. Fortunately, notes Belfort, definitive proof quickly followed his observations. And a Nobel Prize for Cech, along with Yale University's Sidney Altman, followed soon after that. PILE ON THE PROOF: David Sloan Wilson says revolutionary ideas require "extra-strong" support. How much proof is enough? "It's legitimate for researchers to ask for extra-strong proof for an idea that's going to overturn everything," comments David Sloan Wilson, an evolutionary biologist at the State University of New York, Binghamton. Sometimes the evidence is not enough. In 1944, Oswald Avery, Colin MacLeod, and Maclyn McCarty at Rockefeller University in New York offered the first proof that DNA carries and transmits genetic information. The researchers transformed a strain of pneumococci that formed rough colonies to one that formed smooth colonies by adding DNA purified from a smooth strain. But for nearly a decade, opponents argued that the real genetic material was a hearty protein stuck to the DNA samples. "If you're quick on your feet, you can always talk your way around any evidence," says Gunther Stent, a molecular biologist at UC-Berkeley. In fact, Stent argues that the evidence doesn't matter if the theory isn't intuitive. "It's a problem of perception: The brain interprets what it sees in terms of what it knows," he remarks. And in the genetic-material debate, scientists considered DNA too monotonous a molecule to encode the blueprints of life. "Even an idea that is already proven will not be accepted until it can be embedded into our general knowledge," states Stent, a keen observer of delayed recognition (G.S. Stent, Scientific American, 227[6]: 84-93, 1972). But isn't science, by definition, rational? "Scientists hold on to the view that they're very objective," maintains Liebhardt. "But I believe we all have strong biases. People who think they're being totally objective are just fooling themselves." In fact, asserts Wilson, "scientists stick to their paradigms like people stick to religious beliefs." And abandoning the dominant paradigm, according to Kuhn, "is like a undergoing religious conversion," says Stump. As a leading proponent of the theory of evolution called group selection, Wilson has witnessed such conversions. Darwin originally proposed the theory of group selection-which argues that a group of individuals may act as an adaptive unit, working toward the evolutionary benefit of the group-to explain altruistic behavior. Although the theory has been kicking around for a century, Wilson says, it took the efforts of a rock-star promoter to bring it to the attention of serious science journals. Howard Bloom, a Brooklyn-based citizen-scientist and keen observer of human behavior, has professionally handled publicity for the likes of Michael Jackson. After watching music lovers in concert halls, Bloom felt he had witnessed group selection in action. "He had his own vision of humanity operating as a superorganism," says Wilson. "Why not? He spent his life dealing with group psychology, watching jillions of people losing their minds over rock stars." When he became interested in group selection, Bloom recalls, he was horrified to find that scientists were clinging to the notion of individual selection more as gospel than as a theory. He felt his task was clear. "I wanted to get rid of this religious object that was blocking the road of scientific progress," he says. "So I became a catalyst for group selection, acting like a crystal of salt in a supersaturated solution." Bloom turned his publicity prowess toward group selection, gathering all the material, published and unpublished, he could find and forwarding it to writers at Science, Nature, and a number of popular science magazines, including Science News and Natural History. The journalists that Bloom pestered didn't take his word for it, but they did take a closer look at the evidence for group selection, according to Wilson. The data were solid and the researchers credible, but Wilson credits Bloom with attracting some popular press that the theory of group selection might otherwise have missed. Of course, good publicity alone can't drive a revolution. Scientists need money. Cech couldn't have done his work without scientific freedom and research dollars, Belfort points out. "What led to this discovery was the funding that allowed an extremely smart and deliberate researcher to do science that was in no way dictated by programmatic need," she says. RISK-TAKER: Mario Capecchi's revolutionary theory met resistance from funding agencies. Mario Capecchi, a molecular biologist at the University of Utah in Salt Lake City who pioneered gene targeting in mammalian cells, agrees: "When the money gets short, people start to become more cautious. They want to be assured that their work will pay off, because the granting system only rewards success." But Capecchi found ways to get around the funding crunch. The National Institutes of Health initially refused to fund his proposal to study how DNA injected into the nucleus of a mammalian cell incorporated into the native sequence. "They basically said that with 3 x 109 bases in the genome, there was no way this piece of injected DNA could ever find its place in the chromosome," says Capecchi. So he and his colleagues used a bit of creative accounting, shuffling funds from their conventional research to support the more controversial studies. "We realized that if we could get an exogenous piece of DNA to link to its cognate sequence in the chromosome, we could alter genes any way we wanted. If it worked, the payoff would be enormous," he explains. "We weren't doing anything illegal. It's all part of taking risks. Had we failed, all our funding might have been terminated." But their gambit did pay off. Capecchi and his colleagues discovered that mammalian cells possess a huge enzymatic machine that can engineer homologous recombination-a finding that paved the way to the technology of gene targeting and replacement. Proof is good; practical applications, even better. But truly revolutionary ideas often burst onto the scene before all the evidence is in, notes Stent. For example, Barbara McClintock's ideas about jumping genes were considered "sheer lunacy," he says, until microbiologists discovered transposons 15 years later. McClintock, a geneticist at Cold Spring Harbor Laboratory on Long Island, N.Y., eventually received a Nobel Prize for her work on transposable genetic elements. Even if your theory eventually is accepted, how can you avoid being branded a maverick? Dabble, advises Capecchi. "Ideally, you should concentrate on areas where the work is generally accepted, and then do pilot studies in fringe areas," he says. "Once you get an indication that your risky studies are working, then push them hard so you can see some results. "You have to work at the very edge of where the technology is," he suggests. "Risky ventures have bigger payoffs, and bigger losses. But if you don't take risks, you won't get the returns." So you gather your data. You publish. Maybe you even attract funding. But when will your idea gain widespread acceptance in the scientific community? When does a new paradigm bury the popular rival theory and grow roots of its own? Stent's answer is blunt: "When all its opponents die." Karen Hopkin is a freelance science writer based in New York City. She created the "Studmuffins of Science" 1996 calendar and is online at 75110.3626@compuserve.com.

How To Spur Scientific Revolution: Amass Copious Data, Keep It Simple

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