Those who cannot remember the past are condemned to repeat it.
Never forget the importance of history. To know nothing of what happened before you took your place on earth, is to remain a child for ever.
The only thing we learn from history is that we learn nothing from history.
History is like a lantern on the stern, which shines only on the waves behind us.
It is obvious that there are differences of opinion about what can be learned from history. While I personally believe there is much that can be gained from a study of history, I doubt that it can provide all the answers to present problems or is even much help in avoiding past mistakes. I know that it is often said that those who ignore history are destined to repeat it, but it has been my observation that those who know history are just as likely to repeat its mistakes. It is just too easy to focus on the similarities or differences between the past and the present in order to justify some action already decided on. Citing history to justify a course of action is like citing scripture. It is usually self-serving and always selective.
I did not write this historical account because I thought there were some specific lessons to be learned from it. I wrote it because I found the story fascinating and thought others would as well. I was also encouraged by discovering that despite the importance of neurotransmitters for just about everything the brain does, most people know little, if anything, about how they were discovered, the dispute over their existence, the lives of the remarkable scientists involved, or the political events that affected their lives and work.
Despite my reservations about the usefulness of history for providing specific answers to today’s problems, I do believe there is much that it can offer. There is, of course, the enrichment that comes with learning how any body of knowledge has evolved. I recognize that this is a personal reaction, undoubtedly more meaningful to some than to others. However, a knowledge of history helps us appreciate that our current knowledge and convictions are only a moment on a continuum of change. This realization can make us more open to new ideas and less dogmatically certain about what we believe to be true and unchallengeable. Jonathan Cohen, a neuroscientist at Princeton, was recently asked by a reporter why he would want to participate in a symposium on Buddhism and the biology of attention. He replied that:
Neuroscientists want to preserve both the substance and the image of rigor in their approach, so one doesn’t want to be seen as whisking out into the la-la land of studying consciousness. On the other hand, my personal belief is that the history of science has humbled us about the hubris of thinking we know everything.1
Perhaps foremost, a knowledge of history can stimulate us to think about various aspects of any subject in ways that make these reflections richer and more nuanced. Because I have come to believe that this may be the greatest value of history, as distinguished from any pleasure to be derived from an increase in knowledge, I decided to end this book by providing some examples of the thoughts that this history brought to mind for me.
One topic, for example, to which I often found myself returning was how differences in personalities influenced the way this history evolved. Many historians regard individuals as mere “straws in the wind of history,” maintaining that sociopolitical factors shape events and that scientific discoveries are made only after the intellectual ground has been prepared. However, individuals can be significant determinants of when and how events occur and sometimes of whether they even occur at all.
The three central figures in this history, Henry Dale, Otto Loewi, and Walter Cannon, differed greatly in their willingness to speculate and theorize beyond the observable facts. Dale was at one end of the continuum. Although he discovered many of the fundamental facts necessary for proving that neurons secrete neurotransmitters, he was hesitant to theorize about the significance of those facts. He took great care in planning and executing his experiments and in checking his conclusions. His emphasis was on producing replicable results, and I believe it is true that no one ever questioned the reliability of any data he reported. At the same time, however, Dale was a “conservative empiricist,” hesitant to speculate, at least in print, beyond what he believed the evidence definitely proved. Despite the merits of such caution, there is the danger that remaining too close to data may cause the forest to be lost for the trees. Dale was tantalizingly close to discovering chemical neurotransmitters in 1914 when he described the properties that acetylcholine shared with parasympathetic nerve stimulation and how this paralleled what was known about adrenaline and the sympathetic nervous system. Had he been willing to speculate about the significance of his own data, he might well have been encouraged to search for and find that acetylcholine is a natural substance in the body. When Dale (with Dudley) discovered acetylcholine in mammals fifteen years later, he used a methodology that had been available to him as early as 1914. By his own admission, he decided to look for acetylcholine in the body only after Otto Loewi’s speculation and subsequent research had made the possibility of chemical transmission a subject worth pursuing. Seeing may be believing, but being able to see often depends first on believing.
Otto Loewi was much more willing to speculate about chemical transmission, even though his initial evidence was far from convincing. Having speculated about neurohumoral transmission and then been challenged by others, he was motivated to obtain much more compelling evidence in support of his speculation. His willingness to speculate had its own limits, though, and for a number of years he resisted extending his ideas on neurohumoral secretions beyond the nerves that regulate heart rate.
Cannon was at the other end of this continuum. He considered the uncovering of broad integrating concepts to be an essential part of his role as a scientist. When it occurred to him that the different physiological responses evoked by emotional states all prepare animals for “fight or flight,” he seized on this integrating concept and expanded its application. He proposed that chronic exposure to stress could strain and exhaust organs and induce pathological states. Not every fact confirmed his theories. He was wrong on several occasions, for instance when he speculated that the adrenal medulla became exhausted by prolonged stress and lost its capacity to secrete adrenaline. On several occasions he became bogged down in controversy, or at least diverted by it. Cannon may also have missed his opportunity to discover chemical neurotransmitters because he was trying to defend his theory about the importance of adrenaline in coping with stress. However, Cannon’s broad integrating theories, like his ideas about “homeostasis,” stimulated much research and were enormously influential in diverse fields.
While considering the implications of differences in scientific styles, I began to wonder whether there might be an optimal breadth for theories in science. If a theory is too broad it might be stretched so thin that it explains nothing or might need too many ad hoc explanations to support it. This certainly is a possible outcome, but I rejected this thought when I considered Charles Darwin’s theory of evolution. No theory about the natural world is broader in scope than the one Darwin proposed. Although Darwin had collected an enormous amount of supporting evidence for his theory, when it was published he knew virtually nothing about the mechanism of inheritance, and he was wrong in accepting Lamark’s conclusion that acquired characteristics are inherited.2 Even Darwin’s core concept, that evolution works primarily through the selection and survival of the fittest, had to be modified after William Hamilton proposed that “inclusive fitness” shifts the emphasis from survival of individuals to survival of adaptive genes.3 Yet despite the fact that Darwin’s theory was wrong in some respects and incomplete in others, no other theory has had a greater influence on our thinking about the natural world or stimulated more research and discussion in diverse fields. There may be gaps in knowledge and even opposing facts, but proposing the theory often creates the incentive to fill the gaps and determine if troublesome facts really do contradict it.
It is obvious that speculation and theorizing in science involve potential risks as well as gains. It is usually not possible to know in advance which of these will predominate. Trying to support and defend a theory that eventually is proven wrong can involve a substantial loss of time, energy, resources, and, under some circumstances, reputation. Cannon’s and Rosenblueth’s persistence in trying to defend the “two-sympathin theory” is probably an illustrative example of the last. There is also the danger that attempting to support a theory, particularly one that involves some ego investment, can in many subtle ways decrease objectivity in designing experiments and in evaluating the results obtained.
On the positive side, however, mustering support for a theory and defending it against criticism can be exciting and energizing. It can also be a spur to collect the evidence needed to resolve the issue. While Loewi had been a productive and respected pharmacologist before 1921, his proposal that year that neurohumors regulate heart rate had a catalytic effect on his research activity. Following his speculation, Loewi’s research almost immediately acquired a focus and a mobilization of resources that had not been evident previously.
The different scientific styles of Dale, Loewi, and Cannon likely reflect differences in temperament and personality. There is probably some genetic predisposition underlying these differences in temperament, but differences in scientific style are also influenced by mentors and life experiences. Evidence of both influences can be found in this history. The fact that all three made major contributions illustrates that there is no one way to make a significant contribution in science. While this may be obvious, in my experience there are many practicing scientists, and especially mentors of young scientists, who need to be reminded of it.
Another topic this history stimulated me to think more about concerns the dispute over the existence of chemical neurotransmitters and, by extension, the opposition to new ideas in general. There were undoubtedly valid scientific reasons at the time for neurophysiologists to question chemical transmission of the nerve impulse. However, these objections were to a great extent fueled by other than scientific reasons. Some neurophysiologists, for example, resented the intrusion of pharmacologists into what they considered to be their domain. For them, the controversy seemed to be a territorial dispute, and the willingness to accept evidence was often influenced primarily by which side of the argument it helped.
In a number of instances, the arguments in opposition to chemical transmission seemed to reflect a failure to think more imaginatively about what was possible. It will be recalled that many neurophysiologists opposed the concept of chemical transmission because they were convinced that it was too slow a process to evoke the fast responses that occurred at many synapses. However, as Cannon pointed out, little was actually known about how neurotransmitters act on their receptor targets and therefore there was no way of estimating the speed of chemical transmission. Only later was it learned that chemical transmission of the nerve impulse takes only a few milliseconds, fast enough for any task known.
I began to think of other ideas that were rejected prematurely because they were believed to contradict some well-established “fact,” and I recalled a striking example. Once, while I was serving on a National Institute of Mental Health grant committee in the 1960s, we received a proposal from an applicant wanting to pursue some preliminary evidence that brain tissue from a donor animal might facilitate recovery of brain damage in a recipient animal. The applicant thought that the implanted tissue might establish functional connections, and he hypothesized that the adult brain seemed to have more capacity for plasticity and growth than was thought possible at the time. It is embarrassing to recall that the proposal was unanimously rejected with more than a few facetious remarks made about the naiveté of an applicant who did not know that brain neurons are incapable of compensating for damage by new growth. Today, of course, we know otherwise, and a number of laboratories and neurosurgical units are implanting brain tissue and exploring other ways to stimulate nerve growth in experimental animals and human patients. While being aware of such instances should not encourage anyone to abandon their critical acumen, it is possible that such awareness may make some scientists more open to novel ideas and less dogmatic about the reasons for rejecting them.
This history also stimulated me to reflect on the implications of synaptic transmission being chemical rather than electrical. It struck me as ironic that had the “sparks” been right our task of understanding the brain would have been easier. At least there might have been fewer variables to consider if synaptic transmission was purely electrical. While it is true that chemical transmission has opened up many possibilities for influencing brain activity with drugs, this is not as simple a task as often portrayed. According to current estimates, there may be as many as one hundred different chemical substances that affect communication between neurons. Furthermore, the rate of production and release of these different neurotransmitters is constantly changing.4 Moreover, it is now known that most neurons secrete several different neurotransmitters (“co-transmission”), not only one as Dale had concluded. Several different peptide neurotransmitters may even occupy the same synaptic vesicle. Even if the same combination of transmitters is present at all terminals of a given neuron, differences in the receptors at the terminals will produce different results. The number of different receptors known even for a single neurotransmitter is now well beyond anything Dale could have anticipated. At this time, for example, we have discerned at least four different glutamate receptors and six dopamine receptors, and serotonin has at least fifteen different receptors, if all the subtypes are included. Furthermore, there is no assurance that future research will not discover still more receptors.
Neurotransmitter systems are in a constant state of flux. The number and sensitivity of the receptors, for example, is constantly changing, and the effect of neurotransmitters on these receptors depends on the availability of degrading enzymes or the protein carriers responsible for the reuptake of the neurotransmitters. All of these factors vary with different demands on the system. It may appear paradoxical, but as our knowledge increases and we learn more about how all these variables interact, it becomes increasingly difficult to relate any behavioral or physiological effect to a specific neurotransmitter or receptor system. Any intervention, such as the administration of an agonistic or antagonistic drug, no matter how selective its initial target, will inevitably produce a cascading series of physiological changes. Moreover, these changes will affect other neurotransmitter systems in addition to the one initially targeted. All of this knowledge has created exciting possibilities and seemingly endless realms to explore, but also an enormous and sometimes daunting challenge to fully understand or even to predict the outcome of any experimental or clinical intervention.
Still another topic I began to think about while writing this history involves the factors that influence career choices, and I started to reflect about Dale’s deliberation over whether he should accept the position offered by a pharmaceutical company. Over the years I have observed many young scientists who struggled with the same decision. It will be recalled that when Dale was offered a research position in the Wellcome Laboratories his friends advised him not to sell his “scientific birthright for commercial pottage.” The position turned out, however, to be a boon for Dale’s career. Dale was, in part, attracted by the opportunity to obtain a “marriageable income,” but the position also brought with it more support for his research than he would have had in any other position available to him at that point in his career. This support enabled Dale to make such great progress that by the end of the ten years he worked at the Wellcome Laboratory, he was recognized as one of Great Britain’s foremost pharmacologists and was elected to the Royal Society. Of course, Dale had great talent, but he also had the freedom to pursue his scientific interests at the Wellcome Laboratories. In the end, however, he left the company laboratory not only because of other opportunities, but also, in part, because the commercial interests of the company were increasingly interfering with his own scientific interests.
There are today many opportunities for young scientists to work for the pharmaceutical industry, and these positions can be attractive on a number of grounds, most notably the higher salaries and the greater support available for research. However, much has changed since 1904, when Dale started to work at the Wellcome Laboratories. At that time Henry Wellcome was essentially the sole owner of the company and was therefore in a position to back up his inclination to give scientists the freedom to pursue the problems that interested them. This policy attracted a number of outstanding researchers and, in addition to Dale, three other Burroughs Welcome scientists became Nobel Prize recipients.5
The situation is quite different today. Pharmaceutical companies are now huge international corporations, and some of them have an annual income that exceeds the gross national product of a number of countries. These corporations are run by CEOs and boards of directors whose decisions about the research to be pursued are greatly, when not exclusively, influenced by market considerations. Whether this influence of the marketplace turns out to be positive or negative depends primarily on the extent to which the profit motive coincides with worthwhile social and scientific goals.
Over the years, I have followed the careers of young scientists who have gone to work for pharmaceutical companies. It is probably different for established senior scientists, who may be in a position to make some demands before accepting a position with a company. For young scientists starting their careers, however, the decision to go to work for a commercial company carries a much greater risk. It has seemed to me that it has usually worked out best for those young scientists who were not strongly committed to a particular scientific problem and who were quite willing to apply their skills and knowledge to research problems selected by others. Of course, if the problem they are required to work on turns out to interest them and if it can contribute to the development of a useful drug or to scientific knowledge that can be rewarding by itself. It may be recalled that when Dale went to work for the Burroughs Wellcome Company, he was not committed to working on any particular research problem. He started to work on the ergot fungus because Henry Welcome suggested the project, surely in part because of what was thought to be its commercial potential. It was fortunate that ergot contained so many chemical substances that had properties which, in the hands of someone with Dale’s ability, shed light on important physiological processes.
For young scientists strongly committed to a particular line of research the decision to work for a pharmaceutical company can involve a much greater risk. If they are lucky or astute enough to predict the future so that the company and their interest continue to coincide they can benefit from the many advantages already mentioned. Moreover, they will not have to devote the inordinate amount of time academic researchers must invest in order to get funding for their research. However, I have seen many instances where market considerations have led pharmaceutical companies to completely abandon research areas to which they once were committed. This placed young scientists committed to the now abandoned area of research in a difficult position. They often had to chose between giving up their primary research interest or seeking another position, not always an easy task at that juncture in their careers.
Career decisions always involve risks so I suppose the best one can do is to try to make informed guesses about the future. However, young scientists strongly committed to doing research in a specific area need to recognize that there are few “free lunches” in this world. A number of scientists today are electing to join the smaller biotechnology companies as these companies are generally much more committed to pursuing a particular line of research. However, because these companies tend to have “all (or most) of their eggs in one basket,” the risks as well as the potential gains are generally greater. For that reason, the biotech companies tend to attract young scientists who are less “risk aversive.”
These are only a few examples of the many topics that this history caused me to think about. Readers will probably have their own list. There is one additional topic that I want to mention briefly. As I became more and more involved with the lives and work of the scientists involved in this history, I began to think about how fortunate I have been to have spent most of my life in research. For me, this story illustrated much of what is best about such a life. There is, of course, the opportunity to pursue interesting problems and even though they may never be completely solved, it is rewarding to have made a contribution. As this history amply illustrates, life in research can bring you in contact with colleagues around the world. As they traveled, Dale, Loewi, and Cannon often discovered that they actually had friends with common interests who they had never met before. Most researchers have had similar experiences. Although there can be disagreements that are sometimes not pursued in the most constructive manner, this is generally the exception. In general, even disagreements about shared interests often form the basis of lifelong friendships that can enrich one’s life and enhance one’s work. I am not embarrassed to acknowledge that after learning from this history about scientists who unselfishly helped colleagues and who took a stand against some injustice in the world, I was moved to think about my own behavior and how I might have done more.
Finally, although I do not believe that history provides answers to any of today’s problems, I am convinced that it can broaden the way we think about them. Like any good teacher, the value of history is not in the specific lessons it teaches, but in the way it influences how we think about problems.