This is an updated and revised version of an article I wrote for the Lindau Meeting of Nobel laureates and Current Science magazine.
In 1969, one of the more memorable incidents in the public advocacy of science took place. The American physicist Robert Wilson was asked to testify before Congress in support of the construction of the Fermi National Accelerator Laboratory, known as Fermilab. For Wilson, building this huge machine had been a labor of love and nobody had a better background for it. He had worked on the Manhattan Project where he was the youngest group leader in the experimental division, and after the war he had become a professor at Cornell University.
Wilson was a first-rate amateur architect who saw accelerators as works of art. He lovingly designed Fermilab with his own hands and, in order to add to the aesthetic appeal of the place, turned the surrounding acres into a wilderness housing bison and geese. His efforts paid off; Fermilab would become the largest accelerator in the United States and CERN's primary competitor. In 1969 Wilson was asked to justify the expenditure for the multi-million dollar laboratory in front of Congress. The Cold War was raging, most research and especially physics research was being viewed in the context of national security, and Wilson was specifically asked what contribution the new laboratory would make to national defense. He replied in words that should be etched on the foundation stone of every center of basic research. The research, he said, had no direct bearing on national defense. Instead,
"It has only to do with the respect with which we regard one another, the dignity of men, our love of culture. It has to do with: Are we good painters, good sculptors, great poets? I mean all the things we really venerate in our country and are patriotic about. It has nothing to do directly with defending our country except to make it worth defending".
It has nothing to do directly with defending our country except to make it worth defending. In saying these words, Wilson was appealing to the heart of what makes any country great. It is not the fancy cars, the shiny malls, the great financial houses and the cornucopia of industrial food that truly contribute to a country's progress. At one point or another in history, Athens, Florence, Takshashila, Baghdad, Oxford, Gottingen, Copenhagen and Philadelphia were primarily known not for their wealth and the splendor of their monuments but for the unmatched wealth of ideas about science, art, economics, politics, freedom and human dignity that their citizens generated. These ideas are now the bedrock of much of modern civilization. Many of these ideas were solutions to practical problems, but most only sought to explore and push the boundaries of human creativity, curiosity, passion and tolerance. The creators and dreamers of these ideas were less concerned about their practical application and more concerned about their ability to answer questions about human origins and nature, our place in the cosmos and our relationship to other human beings.
Why am I retelling the story of Robert Wilson? Because I believe it strikes at the heart of what these days is fashionably called "translational research". Just like physics research was being viewed through the lens of national defense in the 60s, basic biomedical studies run the risk of being viewed through the lens of translational research in the 2010s. The approach is clearly not popular among leading researchers. In 2009, Nobel Laureate Martin Chalfie gave a talk at the Lindau Meeting in which he described the great satisfaction he had gotten from doing non-translational research. Chalfie is not alone; last year I attended a lecture by another Nobel Laureate, Thomas Steitz. Steitz who won the prize for cracking open the structure of the ribosome proudly announced at the beginning of the talk that "the only kind of translation I have worked on is that orchestrated by the ribosome". And this week in Science magazine, Nobel Laureates Joseph Goldstein and Michael Brown lament the passing of the golden age of basic research at the NIH - an era which produced nine Nobel Prize winners during a single decade. As Goldstein and Brown put it, “translational research relegates basic science to a back burner…individual curiosity-driven science has been replaced by large consortia dedicated to the proposition that gathering vast amounts of correlative data will somehow provide an answer to life’s fundamental questions”.
So what is translational research? Many definitions seem to abound and Wikipedia seems to be as good a guide as any: "Translational research is a way of thinking about and conducting scientific research to make the results of research applicable to the population under study and is practised in the natural and biological, behavioural, and social sciences". The goal of translational research especially in medicine seems to transform basic biomedical research discoveries from "bench to bedside".
In the last few years this kind of thinking has has swamped the public discourse on science. New centers are being founded and funded whose mandate is to translate basic research into products directly benefiting humanity. The NIH, the largest biomedical research agency in the world, has also embraced a new National Center for Advancing Translational Research. The director of the NIH, Francis Collins, has not tired of pointing out the exciting advances in discovering new drugs which would be made possible by harnessing data from the human genome project. Not surprisingly, the press has eagerly jumped on the bandwagon, with reports pitching translational research and personalized medicine regularly appearing in the nation's leading papers. Echoing leading scientists, the press seems to be telling us that we should all look forward to supporting translational research in its various guises.
All this makes the idea of translational research sound promising. And yet there must be a good reason why distinguished Nobel Prize winners like Chalfie, Steitz, Goldstein and Brown bristle at the mention of translational research. The reason is actually not too hard to discern. The problem is not with applied research per se. Nobody can doubt that applied research especially done by the pharmaceutical and biotechnology industries has saved innumerable lives in the last one hundred years. As Pasteur said, "there is science and the applications of science", and he saw them lying on a continuum. No, there is nothing wrong with trying to turn basic ideas into applied products.
What is wrong is that translational research is being seen as a panacea that will address the flagging rate of new biomedical advances. The thinking seems to declare that if only more people were given more money and deliberately focused on direct application, we would suddenly see a windfall of new therapies against disease. This thinking suffers from two major problems.
The first problem is that history is not really on the side of translational research. Most inventions and practical applications of science and technology which we take for granted have come not from people sitting in a room trying to invent new things but as fortuitous offshoots of curiosity-driven research. Penicillin was discovered through serendipity by a most alert Alexander Fleming who was trying to plate bacterial cultures, not one trying to actually discover the next breakthrough antibiotic. Nuclear Magnetic Resonance (which in turn led to MRI) was discovered by physicists who were interrogating the properties of atoms using magnetic fields, not ones who were trying to find a method for determining the structures of organic and biological molecules. The discovery of most drugs built upon basic discoveries about human physiology and anatomy made by physicians and researchers who were simply trying to find more about how the body works. As Goldstein and Brown describe in their Science opinion piece, NIH scientists in the 60s focused on basic questions involving receptors and cancer cells, but this work had an immense impact on drug discovery; for instance, heart disease-preventing statins which are the world’s best-selling drugs derive directly from Goldstein and Brown’s pioneering work on cholesterol metabolism. Examples also proliferate other disciplines; the Charged-Coupled Device (CCD), lasers, microwaves, computers and the World Wide Web are all fruits of basic and not targeted research.
If the history of science teaches us anything, it is that curiosity-driven basic research has paid the highest dividends in terms of practical inventions and advances. Tinkering, somewhat aimless but enthusiastic exploration of biological and physical systems and following one's nose have been the ingredients for some of the key inventions that have transformed our lives. Radar, computers, drugs, detergents, plastics and microwave ovens were all made possible not because someone sat down and tried to discover them but because they arose as fortuitous consequences of elemental, pure research. The hype of translational research not only deflects attention from curiosity-driven basic research but also creates the illusion - and dangerously so especially in the minds of young scientists - that asking people to discover new things is the best way to generate new ideas. In fact, trying to discover new things by forcing people to discover them will only siphon off funds from those who have the actual capability of discovering these things. This is especially damning for bright young researchers who are trying to survive in an increasingly straitjacketed research milieu.
The second more practical but equally important problem with translational research is that it puts the cart before the horse. First come the ideas; then come the applications. There is nothing fundamentally wrong with trying to build a focused institute to discover a drug, say, for schizophrenia. But doing this when most of the basic neuropharmacology, biochemistry and genetics of schizophrenia are unknown is a great diversion of focus and funds. Before we can apply basic knowledge, let's first make sure that the knowledge exists. Efforts based on incomplete knowledge would only result in a great squandering of manpower, intellectual and financial resources. Such misapplication of resources seems to be the major problem for instance with a new center for drug discovery that the NIH plans to establish. The NIH seeks to channel the newfound data on the human genome to discover new drugs for personalized medicine. This is a laudable goal, but the problem is that we still have miles to go before we truly understand the basic implications of genomic data. It is only recently that we have started to become aware of the "post-genomic" universe of epigenetics and signal transduction. We have barely started to scratch the surface of the myriad ways in which genomic sequences are massaged and manipulated to produce the complex set of physiological events involved in disease and health.
And all this does not even consider the actual workings of proteins and small molecules in mediating key biological events, something which is underlined by genetics but which constitutes a whole new level of emergent complexity. In the absence of all this basic knowledge which is just emerging, how pertinent is it to launch a concerted effort to discover new drugs based on this vastly incomplete knowledge? It would be like trying to construct a skyscraper without fully understanding the properties of bricks and cement.
Chalfie, Steitz and others like them are also right to criticize the frenzy that translational research generates in the popular press. We live in an age when buzzwords are eagerly generated and assimilated by the media. These buzzwords usually run roughshod over subtleties and ambiguities and the press seldom has a taste for indulging these in the first place. Needless to say, committing national resources and public attention to translational research when most of the basics are still to be understood is an endeavor fraught with great risk and uncertainty. It would be far wiser to bolster basic research that can bring us to the brink of real application. There are places where such research is conducted. They are called universities.
Ultimately, the importance of basic research goes back to what Robert Wilson said to Congress. It has to do with the same reasons that we created the Mona Lisa, painted the Sistine Chapel, built Chartres Cathedral, wrote The Love Song of J. Alfred Prufrock and composed the Goldberg Variations. Da Vinci, Michelangelo, T. S. Eliot and Bach were all trying to find the essence of man's soul and his relationship with the universe and with his fellow men. So were Einstein, Newton, Faraday and Darwin. They were not trying to invent a better mousetrap, but the world did beat a path to their door. Similarly, once our basic understanding of biological systems is firmly in place, translation will willingly follow. The next researcher, when asked to comment on the relevance of his or her basic studies in cell biology to translational research, should echo Wilson: "It has nothing to do directly with translational research, except to enable it".