Early exploration of the visual cortex.

As we look back over the period of the 60s and 70s what stands out most in our minds is the fun we had. We came into a new field and seemed to have carte blanche to do whatever we liked. What in retrospect mainly characterized our styles was a technical simplicity, amounting almost to sloppiness, and a relative freedom from theoretical constraints. We hesitated to invest heavily in a technique until it became very clear that we really needed it. In the case of the Nauta method and the acquisition of a histological technician, the investment paid off. An investment in an electron microscope near the end of the 60s failed when we lost interest in obtaining sharp pictures, and the instrument gathered dust. We were very late to adopt the use of computers: our research may have suffered as a consequence. It is impossible to assess the trade-off between whatever we missed and the time it would have taken to learn to do the programming. Meanwhile we were also spared the drawing of graphs and statistical evaluations for which computers are so useful.In 1960, theories as to how the central nervous system might work seemed to us to be contributing little to understanding the brain; we inserted our electrodes with no major preconceived ideas as to what to expect. We did have a vague faith that it was the connections that counted, and the assurance, mainly from the work of Ramon y Cajal, that the connections were orderly and beautiful, with little element of randomness. As the decade progressed, new theoretical constructs—that the brain was a Fourier analyzer, that linear systems analysis had something to offer, that Gabor functions or Gaussians were worth knowing about—seemed wild to us, to the extent that we could understand the ideas at all. At times we have felt alone in this conservatism, but we are encouraged when we reflect on how free such fields as evolution and molecular biology have been from such heavily computational approaches. This is not to deny the importance of theory to fields such as physics or even some aspects of biology, but only to suggest that each field has its own style, and that either theory has a different and lesser part to play in neurobiology, or that neurobiology is not quite ready for a mathematical approach.Today we are struck by several huge differences between now and the 60s. The field has expanded out of all recognition; we go to meetings of the Society for Neuroscience, now with registrations of 25,000, compared to a few hundred in the 60s; during the meeting, every day there are one or two sessions on V1 alone and one or two on visual deprivation. While the field has grown, so has its financial support, but not in proportion, so we have the strong feeling that we were active at the right time, with enough money for our research and far less anxiety. We don't envy the competition young neurobiologists face, or the time they have to squander writing grant applications.Directions of brain research have changed, not surprisingly. Two powerful trends have taken off in opposite directions. First, and most prominent in terms of resources, is the push toward the cellular and molecular levels. One has the feeling that this movement is represented by 23,000 of the 25,000 who attend our annual meetings. No one could possibly deny the importance of the knowledge that is coming out of this emphasis. At the other extreme, and just as important, much of the work done today in the central visual system is in awake, behaving animals, especially monkeys. As a consequence, in vision inroads are rapidly being made into the two dozen or so visual areas that used to be called “area 19”, to say nothing of vision-related areas in temporal, parietal, and frontal lobes. Each area can be investigated without the disruption that anesthesia causes to the firing of cells, and to behavior. It now is accepted that beyond the primary visual area and V2, the pathway diverges into subdivisions in which quite different aspects of vision are handled—form, movement, color, stereopsis, and so on. This does not mean the absence of any hierarchical organization; on the contrary it implies many hierarchies working in parallel. Best of all, perhaps, the style of working in awake, behaving animals involves recording not in stints of 24–36 hours, or till one collapses from exhaustion, but for just a few hours a day, or until the monkey gets fed up with fruit juice.Meanwhile we confess to a nostalgia for the approach we took during those 25 years from 1958 on, in which we worked at a level that asked about the detailed functional organization of cortex: the repertoires of cells of different classes, the layers and the columns. We feel nostalgia not just for old times' sake, but because the work is so fascinating and there is so much still to do. Area 17 is off to a good start (we hope); 18 (V2) with its thick, thin, and pale stripes, is known in about the same sketchy detail as 17 was in 1970; in MT we know a lot about function, thanks to Zeki, Movshon, Newsome, Born, and others, and we know of several column types. But for most of the other few dozen areas we have little of this kind of knowledge. Awake-behaving techniques, powerful as they are, haven't so far lent themselves to the coupling of physiology and anatomy that is required for getting at functional organization, and so functional organization is languishing. We hope that in the future technical advances will make it possible to combine the two approaches.Fields of research are subject to fashions. At present, the detailed (some would say, plodding!) area-by-area analysis is being eclipsed by the excitement and vigor of work at the molecular and awake-behaving levels. That is as it should be, because research has to be done by people who are excited by what they are doing and find it fun. Meanwhile the problems in detailed organization will still be waiting to be taken up again when the interest revives.‡To whom correspondence should be addressed.