Brain and Visual Perception: The Story of a 25-Year Collaboration

Torsten Wiesel and David Hubel worked to determine how nerve cells turned visual stimuli into images in the brain. For that work they shared the Nobel Prize for medicine in 1981. (Image: Golden Goose Award / CC)

Excerpt from Brain and Visual Perception: The Story of a 25-Year Collaboration, by Nobel Laureates David H. Hubel and Torsten N. Wiesel (Oxford University Press, 2004). Reprinted with permission from the authors.

Chapter 28: Epilogue: Summing Up

Perhaps the most remarkable thing about our collaboration is the fact that it continued for 25 years, much longer than most collaborations. Ours had the special quality that it was between equals, in age and in seniority. Our two abilities were not identical but were complementary. An analogy might be Gilbert and Sullivan (Steve Kuffler once jokingly compared us to Huntley and Brinkley). Rosencrantz and Guildenstern also come to mind. As we look back, what stands out is the almost total absence of disagreements. When, late at night, should we finally quit and go home? Whom among fellow scientists did we revere or otherwise? What should we do next? We never quite knew or even discussed where our ideas came from: they presumably arose in the long discussions that went on during our interminable experiments, and once an idea was hatched by one of us it was often forgotten, only to be resurrected months later by the other.

Almost absent from our way of working and thinking were hypotheses, at least explicit ones. We regarded our work as mainly exploratory, and although some experiments were done to answer specific questions, most were done in the spirit of Columbus crossing the Atlantic to see what he would find. Today our grant proposals would surely be criticized as not being “hypothesis driven”, as not following the rules of Science as taught in high school and as exemplified especially in physics. We believe that such rules as to how Science (with a capital S) is done, or should be done, are largely fiction, an attempt to retrospectively codify a process that often amounts to groping. There simply are no rules as to how to do science. Looking back, we can recognize times when we must have had something vaguely resembling a “hypothesis”. Probably we could have dressed up our thought processes in those terms, but we would have found it dishonest to do so, even for grant-application purposes. Similarly, the way scientific papers are written usually represents a kind of fiction in rearranging the order in which ideas occur and the work is done, to form a logical sequence that may have little basis in reality. Papers written in the 1800s are often more open and honest (if that is the right word) in saying how ideas developed. In our papers we tried to preserve some of that and even succeeded in inserting a few jokes, if only to prove that the reviewers had occasional lapses of attention. Above all we tried to make our papers easy to read. With almost religious determination we avoided abbreviations, with the sole exceptions of LGB and EPSP. That avoidance probably cost the publishers all of three extra lines at the end of some of our papers, but it must have saved our readers many minutes of searching back to find what the letters stood for. We tried to make our illustrations easy to read by resisting the temptation to combine eighteen small figures into one large one, a custom perhaps started by Eccles and perpetuated by Eric Kandel. We tried to avoid figure-legends in which the a’s, b’s and c’s are buried in text instead of being separated by paragraphs, so that the poor reader has to search for the tiny letters with a dissecting microscope. We were often unsuccessful because of the puzzling resistance of editors. All this was in attempts to make our papers less tiring and tiresome to read: we hope we succeeded.

How do we find our field today, in comparison with its state when we set out on this adventure in 1958? We set out at a perfect time. Virtually nothing had been done with microelectrodes in the visual cortex—or in the cortex in general, except for Mountcastle’s marvelous beginning in the somatosensory cortex. We had the necessary techniques—or we had the leisure to develop them ourselves. A little earlier and we might have ended up studying impulses and synapses, or possibly the spinal cord, which was very popular in the 1950s. In the visual cortex we had little competition for about ten years, perhaps because it was generally felt that our type of work was too arduous, or perhaps because it was assumed that you had to understand the retina perfectly before going more centrally. Something like that certainly happened in the auditory system, in which the research got hung up on the end organ, and the auditory cortex was, and still is, relatively neglected.

Today we have some concerns about the present state of our field. One unfortunate development is the fading of neuroanatomy. Our work, at least much of it, involved a close coupling of physiology and neuroanatomy, and in the 1970s we were doing about as much of one as of the other. We certainly were lucky in inheriting techniques like the Nauta method and autoradiography—or one might say we were good at ignoring those who said that only the experts should attempt them. Typically we used a monkey each week, often doing separate physiological and anatomical studies in the same monkey. That allowed us to work out much of the structural and physiological relationships that are so important in understanding the cortex. We were also lucky in working at a time before the animal rights groups had made it so much harder to do research involving animals—harder in the sense of expenses and the hoops to be jumped through to get past all the layers of red tape that exist today. Monkeys are now many times more expensive, and the hoops are more numerous. To use monkeys today at the rate we used them in the 1970s and 1980s would be almost impossible.

We were lucky in having youth on our side. Today we certainly would not have the stamina to stay up all night, even once a week. For all these reasons the field has turned increasingly to the use of awake-behaving chronically implanted monkeys, in which one monkey can be recorded from for months or years, and one can work for four hours each day and then go home to dinner. The catch is that parallel anatomical studies are practically impossible because the brain becomes available only after many months, and has been recorded from so many times that it resembles a pincushion.

A second, in some ways unfortunate, trend in visual-cortex physiology is its increasing popularity, with hundreds of labs working in dozens of the known visual cortical areas. So the competition is greater, by orders of magnitude. We do not fully understand why, in the realm of systems physiology, vision should have become so dominant, relative to other systems. To some extent it probably is a bandwagon effect: when a field becomes trendy, people stream in from all sides, as happened many years ago in the case of the bolo-bat and the hula hoop. When we started out, the most dynamic branch of sensory neurophysiology was somatosensory, thanks to Clinton Woolsey and especially Vernon Mountcastle. The switch over to vision, while hard to explain, could have been related to the high information content of vision, relative to touch and joint position. If that is the reason, then it is hard to see why the central auditory path is so neglected.

A third problem represents to us an example of illnesses that scientific fields can be subject to. In neurophysiology this is the increasing popularity of theory, sometimes called computation. No one familiar with developments in physics in the past century or so could possibly deny the importance of theory in that branch of science. But it seems to us that the chances of theory ever assuming a comparable importance in biology (and in particular, neurobiology) may be slim. One indeed has the impression that the main proponents of theory in neurophysiology may be scientists who have trained in mathematics and, having gone into biology, are reluctant to give up the mathematics. I can understand that, having had some training in mathematics and once having expected to use it in neurophysiology. In the best hands (and one thinks of people such as David Marr, Horace Barlow, Werner Reichardt, Terry Sejnowski, Christof Koch and Francis Crick), our field has certainly benefited. But in the case of such subjects as “linear systems analysis,” the emphasis seems either puzzling or wrong. No one with much experience with cortical cells could think of them in any real sense as linear. Our feelings concerning the use of sine-wave gratings, already referred to here and there in this book, always in a pejorative way, will come as no surprise to readers who have put up with our dogmatism thus far. Another hot topic in recent years has been “multiplexing”, the notion that a cell’s responses can reflect its involvement with a multitude of variables, and that few if any cells are highly specialized. Visual scientists who are in any way burdened with a familiarity with cells in the visual cortex of higher mammals will be astonished at the idea that all cells carry information about all variables (such as orientation, movement direction, color, spatial frequency, and stereopsis). What has struck us from the very first was the increasing degree of specialization of cells as one goes from level to level in the central nervous system, and the specialization already apparent in most cells in V-l. We have double-opponent cells with their color and center-surround selectivity and their lack of orientation selectivity; the sharp orientation selectivity of most other cells in V-l (outside layer 4) along with their frequent movement-direction selectivity, but with an almost total lack of concern with color; cells that respond to black slits but not to white, or the reverse; or those that respond to both black and white; or those that respond to red slits, but neither black nor white. Multiplexing seems to imply a small amount of specialization for many variables, with the sorting out presumably being left to later stages in the nervous system, if it occurs at all. The idea is ingenious but seems not to be used very much by the brain. Of course we have many examples of a cell’s encoding more than one variable: cells involved with stereopsis seem always to be orientation selective; most V-l color-coded cells have center-surround fields, but to lack orientation selectivity. Most cells indeed seem to encode an assortment of variables, but a very limited assortment. What we do not see is a small degree of specialization for many or all possible variables.

The field of molecular biology, which we regard as more successful as a science than our field, seems largely to have avoided being beset with computation. In The Molecular Biology of the Gene I look in vain for equations. No one has tried to fit a protein molecule to a Gabor function, as far as I know. One could be terribly wrong about such things, and it will be interesting to see how our field develops. I do sense that fields of science, like biological organisms, can become sick, and I hope that does not happen to neurophysiology.

Why did we at last stop collaborating, around 1980? The prize came in 1981, so that event must have been unrelated. Forces promoting our separation had been present from an early time—even our staunchest supporter, Steve Kuffler, repeatedly and gently suggested we might be wise to split and each take on postdoctoral collaborators and different projects. But always in the end we had complete support from Steve to go on stubbornly working together. As time went on, the main force towards separation was increasing pressure to do administration and teaching that we could not entirely avoid. I had had a dose of being a department head, and stood it for a year, giving up when it became clear that the installation of a pencil-sharpener in the physiology department secretary’s office required me to discuss the matter over coffee with each of the other tenure department members. In 1973 Steve Kuffler, having been leader of our group since its inception at Johns Hopkins and chairman since the neurobiology department’s founding in 1966, decided to step down. A successor had to be found; I had learned my lesson, but Torsten was a sitting duck and too conscientious to refuse. While the department was still young and small, the administration was relatively light, but as it got bigger, with more faculty and graduate students, the drain on his time increased. It got so that our customary Tuesday experiments were being done without prior planning and with little subsequent discussion. In the end we felt like two horses continuing to drag the same plough over the same terrain year after year, with constant guilt feelings that we were neglecting one or another committee or were getting behind in letters of recommendation.

We are nevertheless grateful at having had so many years of uninterrupted research. We were wise enough, perhaps, to avoid the usual trap of taking on many dependent postdocs and graduate students, gradually letting them do more and more of the research we enjoyed, while we spent more and more time at the desk writing papers, grant requests and letters of recommendation, and losing our feel for the research. We did have small numbers of postdocs and graduate students, but made them independent, giving advice gently and rarely, as Steve had done with us. That way, we felt, we did not deprive them of the main thing a beginning scientist needs to learn: to get one’s own ideas and try them out. The strategy worked, for our trainees (if that is the right word!) have done well.

From 1980 to 1990 I collaborated with Margaret Livingstone, who had begun as a graduate student in our department, in a study of color and stereopsis in V-2. We carried on a regular dialogue with Edwin Land, whom Torsten and I had gotten to know in the 1970s and 1980s. I greatly admired his inventiveness, and his death, in 1991, came as a severe blow.

I then collaborated with Stephen Macknik and Susana Martinez-Conde on a study of microsaccadic eye movements and the bursts of firing they produce in cells in the primary visual cortex. Finally, with a fellow Canadian, Kevin Duffy, I have been looking at receptive fields in the striate cortex of dark-adapted monkeys.

Today I run a class for 12 freshman Harvard College undergraduates, with weekly discussions and a lab. In their first semester at college their enthusiasm over starting college has not yet worn off, and these seminars have been my best teaching experience in 45 years of university life. The program was founded years ago by Edwin Land, motivated by his disaffection over having had so little contact with his professors when he was a student at Harvard.

We must end by saying words of thanks to the society that supported us. We were most fortunate that the National Institutes of Health existed and that the Eye Institute came into being at just about the time we started. And especially that the members of the NIH Eye Institute were so supportive and such a pleasure to work with. The other piece of luck was everything about the university system of the United States, especially the relative freedom from domination by department heads, particularly in handling one’s finances; the freedom to move to some other place if not satisfied, and perhaps above all the wonderful enthusiasm and overall quality of the students. These are all things that explain the success of biological research in this country, and to a large extent explain its lack of success in other countries, even wealthy ones. We have, and do, complain loudly about many problems this country has had and still has—the swings in politics such as the McCarthy and Nixon eras, Vietnam, and prevailing attitudes to the Kyoto Accord, the World Court, Iraq, the gun lobby, and so on. But about the handsome way our research and our fellow biologists’ research has been supported we have only gratitude.

Excerpted from Brain and Visual Perception by Nobel Laureates David H. Hubel and Torsten N. Wiesel. Copyright © Oxford University Press, 2005. All rights reserved.

David H. Hubel is the John Franklin Enders Professor of Neurobiology, Emeritus, at Harvard Medical School. Dr. Hubel retired in 2000 from his University Professorship at Harvard, but continues to do full-time research and teaching at Harvard Medical School. His research at present is on the subject of steropsis in pre-striate cortical regions in monkeys. He teaches a full course each fall term to a group of twelve Harvard first-year undergraduate students, and is advisor to several graduate students and postdoctoral fellows. He has been described as one of the major medical scientists of the latter twentieth century.

Torsten N. Wiesel is Director of the Shelby White and Leon Levy Center for Mind, Brain and Behavior and President Emeritus of Rockefeller University. Dr. Wiesel has done much work as a global human rights advocate. He served for 10 years (1994-2004) as chair of the Committee of Human Rights of the National Academies of Science in the U.S.A., as well as the International Human Rights Network of Academies and Scholarly Societies. He is a founding member of the Israeli-Palestinian Science Organization, a nongovernmental nonprofit established in 2004 to support collaborative research between scientists in Israel and Palestine.

The authors were both awarded the 1981 Nobel Prize in Physiology or Medicine in recognition of their pioneering work on the neural basis of visual perception, carried out at Harvard Medical School. Their discoveries have provided a greater understanding of brain development in the critical early stages of human development following birth. Their research opened the door for the understanding and treatment of childhood cataracts and strabismus. They were also important in the study of cortical plasticity. Thanks to their work, the visual cortex has become the best known part of the brain.

David Hubel and Torsten Wiesel 1981 Nobel Prize

Dr. David Hubel

Torsten Wiesel (Rockefeller University): Exploring the Visual Brain

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