Patricia Smith Churchland

Philosophy Department, University of California, San Diego

As an academic, one shoulders an assortment of duties. These duties have different “hedonic scores,” to put it in limbic system terms. Some of these duties involve grading marginally comprehensible and humorless term papers; some duties require that we hector brilliant but foot-dragging graduate students to cross the dissertation finish line. Yet other duties involve the tedium of the legendary department meeting, grinding on until the last dog has been hanged. By contrast, my duty here has a high hedonic score. So much so, that I hesitate to consider this brief commentary a duty at all.

From whatever direction we look at it, the awarding of the McDonnell Centennial Fellowships merits unalloyed glee. Each fellow has, after all, been awarded $1 million to pursue the intellectual adventure of his or her dreams. In addition, the award program is, I think, important for the particular flag it runs up the research flagpole. And that is the flag of the unconventional and unorthodox, the daring and risky, the not-yet gray, and the not yet medaled. An initiative such as the McDonnell Foundation Centennial Fellowship Program is important because, truly to thrive, science must nurture the intellectually adventurous.

Thomas Kuhn described science as predominantly paradigm governed, by which he meant that subfields have a kind of conventional wisdom that functions rather like a powerful gravitational well. The practitioners within the subfield tend to promote, and encourage, and fund those

people whose projects and research essentially conform to the conventional wisdom prevailing in their subfield. Occasionally, against considerable odds, with considerable luck, and to considerable consternation, highly original ideas emerge to challenge the prevailing orthodoxy dominating a particular field of science. The pressures to acquiesce in the conventional wisdom, to work within it, further it, and confirm it, are, however, enormous. They exist at every level, from grammar school, college, graduate school, and all the way through the academic ranks. By and large, beautiful and brilliant science does indeed get done within the confines of the governing paradigm. Moreover, it is fair to say that progress would be hindered if kicking over the traces were the norm, rather than the “abnorm,” as it were.

Making it too easy for the unconventional can, I have no doubt, result in a superabundance of cranks and crackpots—of visionaries with lots of vision but precious little common sense. Too much of a good thing may not, despite Mae West’s winking assurances, be wonderful. Nevertheless, risky research is desirable if we are to unseat assumptions that are not so much proved as conventionally respected, not so much true as “taken to be true.” When working assumptions go unquestioned, they tend to become dogma, however wrong they may be. What might have served well enough as a convenient fiction becomes, when canonized as fact, an obstacle to further progress. The trouble is, therefore, funding for the unorthodox researcher and his or her unorthodox hypotheses remains an ongoing challenge for the standard funding institutions, who by their very nature, rarely, if reasonably, support anything other than center-of-the-road projects.

Especially gratifying it is, therefore, that the McDonnell Centennial Fellowship Program was set up to reward the innovative and frisky who could undertake risky and surprising projects without kowtowing to the conventionally wise graybeards. It is all the more appropriate, given that the founder, James S. McDonnell, was himself a maverick, a man of genuine intellectual vision and courage. He knew very well the value of having the chance to develop an idea whose potential others were too timid or too rigid to see.

My recollection is that the inspiration for the Centennial Fellowship Program originated with Susan Fitzpatrick, and she deserves much credit for not only hatching the general idea, but for guiding it through the many delicate stages that brought us to this point, where we may rejoice with those chosen to receive McDonnell Centennial Fellowships. Many other people, including members of the McDonnell family and John Bruer, were of course crucial to the program’s success, and we are in their debt.

I turn now to make several brief remarks about cognitive neuroscience in general. Were one to judge solely by what appears in the scientific

journals and at scientific meetings, cognitive neuroscience is a research juggernaut plowing unswervingly and surefootedly forward. If you don’t look too closely, it may seem that the basic framework for understanding how the brain works is essentially in place. It may seem that by and large most future neuroscience is pretty much a matter of filling in the details in a framework that is otherwise sturdy and established. But this appearance is largely an illusion.

Although more progress has been made in the past two decades in neuroscience than in all the rest of human history, neuroscience has yet to win its wings as a mature science. In this sense, neuroscience is rather like physics before Newton or chemistry before Dalton or molecular biology before Crick and Watson. That is, neuroscience cannot yet boast anything like an explanatory exoskeleton within which we can be reasonably confident that we are asking the right questions and using concepts that are empirically grounded and robustly defined. Molecular biology and cell biology, by contrast, do have considerable explanatory exoskeleton in place. Arguably, surprises still await us in these subfields, yet the general mechanisms governing the target phenomena are uncontestably better determined than in neuroscience.

This state of affairs does not mean that neuroscientists have been shiftless or remiss in some respect. Rather, it reflects the unavoidable problems inherent in understanding something as complex and conceptually alien as a nervous system. Moreover, neuroscience is likely to achieve maturity later than the other subfields, not just because it is harder —though it undoubtedly is—but also because it heavily depends on results in those other fields, as well as on technology made possible by very recent developments in physics and engineering.

When in grant-funding or paper-reviewing mode, we often have to pretend that the appearance of solidity is the reality. For sound pragmatic reasons, we pretend that there is a more or less well-established explanatory framework whose basic concepts are empirically well grounded and well understood. Hence we may assume, for example, that in nervous systems, learning mechanisms are known to be Hebbian, or that the spike is the only neuronal event that codes information. Allowed freely to reflect and ponder, we grudgingly suspect it isn’t really so.

My students are shocked to be reminded that we do not in fact understand how neurons code information, or even how to distinguish neurons that code information from neurons that are doing something else, such as housekeeping or neuromodulation or something entirely “else. ” In fact, we do not have a concept of “information” that is suitable to what goes on in nervous systems. The Shannon –Weaver concept of information, designed for the context of communication lines, is not even roughly appropriate to our needs in neuroscience. “Information” and the “pro-

cessing of information” are indispensable concepts in neuroscience, yet they lack theoretical and empirical infrastructure, much as the notion of “momentum” did before Newton or “gene” before 1953. Experiments make it clear that it is essential to talk about the brain as representing various things, such as the position of the limbs or a location in physical space, but we do not really understand what we need to mean by “representation.” Nor do we understand how to integrate representational descriptions (e.g., “is a representation of a face”) with causal descriptions (e.g., “is hungry”).

This is only for starters. In addition, we do not understand how nervous systems exploit time to achieve cognitive and behavioral results. We do not understand how nervous systems integrate signals over time so that they can recognize a temporally extended pattern such as a bird song or a sentence. Yet the timing of neuronal events seems to be absolutely crucial to just about everything a nervous system does. We do not know how movements can be sequenced or how sequences can be modified or how movement decisions are made. We do not know the extent to which mammalian nervous systems are input-output devices and the extent to which their activity is intrinsic in a way utterly different from any known computer. We do not know why we sleep and dream, what sensory images are, and how the appropriate ones come into being when needed.

Despite confident announcements in evolutionary psychology about genes “for” this and that mental capacity, in fact we do not know what or how much of the neuronal structure in mammals is genetically specified, although simple arithmetic tells us that it cannot be specified synapse by synapse. Specialization of structure does of course exist in nervous systems, but the nature and degree of top-down influence in perception remains unclear, as does cross-modal integration and cognitive coherence. Whether nervous systems have modules, in the sense that some psychologists define the word, looks highly unlikely, although how to characterize an area of specialization, if it is not a “module” in the classical sense, is puzzling. The puzzle will not be resolved merely by cobbling together some precise definition. To serve a scientific purpose, the definition has to grow out of the empirical facts of the matter, and many relevant facts we just do not have our hands on yet. Virtually every example of modularity (in the classical sense) that has ever been explored turns out, when experiments alter the developmental conditions, not to be a modular entity except in the most attenuated of senses. And, to continue, we do not know what functions are performed by the massive numbers of back projections known to exist just about everywhere.

This is a lot not to know. And it highlights the need for an explanatory exoskeleton adequate to these issues. Partly, because the profound, exoskeletal questions remain, neuroscience is both tremendously exciting

and also faintly exasperating. Sometimes one is moved to wonder whether we are asking the neural equivalent of what makes the crystal spheres turn or what the weight of phlogiston is or why God decided to make disease a punishment for sin. In his opening remarks at the 1999 Centennial Fellowship Symposium, Endel Tulving warned that our common sense—our intuitive hunches—about what the brain is doing and how it is doing it are, in many cases, going to be flat-out wrong. I share Tulving’s prediction, and it is tantalizing to wonder just how hypotheses and theories in cognitive neuroscience will look 100 years from now.

My handful of neuroscience questions is unsystematically presented and insufficiently developed, but my intent here is merely to convey a simple point: There is a great deal of f oundational science that is still to be done on nervous systems. By emphasizing questions as opposed to answers, I emphatically do not mean to diminish the brilliant progress in neuroscience. Certainly, much about the basic components—neurons—has been discovered; and without these discoveries, functional questions about how we see, plan, decide, and move could not fruitfully proceed. Much about the anatomy and the physiology at the systems level has also been discovered. That too is absolutely essential groundwork. I have no wish to chastise neuroscience. Rather, I want affectionately to view it at arm’s length and to cheer on those who are willing to tackle some of the exoskeletal questions. Because there is much of a fundamental nature that we do not know about the brain, there is a lot of frontier territory. There is still room—and need—for pioneers.