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Scientific Discoveries: What Is Required for Lasting Impact Annual Review of Physiology Vol. 78:1-21 (Volume publication date February 2016) First published online as a Review in Advance on August 13, 2015 https://doi.org/10.1146/annurev-physiol-021115-105257 (https://doi.org/10.1146/annurev-physiol-021115-105257)

Terje Lømo Institute of Basic Medical Sciences, University of Oslo, 0317 Oslo, Norway; email: [email protected] (mailto:[email protected])



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Sections ABSTRACT KEYWORDS INTRODUCTION THE DISCOVERY OF LTP IMPULSE ACTIVITY CONTROLS THE PHENOTYPE OF MUSCLE FIBERS THE RECEPTION AND LONG-TERM IMPACT OF THE TWO DISCOVERIES CONCLUSION DISCLOSURE STATEMENT ACKNOWLEDGMENTS LITERATURE CITED

Abstract I have been involved in two scientific discoveries of some impact. One is the discovery of long-term potentiation (LTP), the phenomenon that brief, highfrequency impulse activity at synapses in the brain can lead to long-lasting increases in their efficiency of transmission. This finding demonstrated that synapses are plastic, a property thought to be necessary for learning and memory. The other discovery is that nerve-evoked muscle impulse activity, rather than putative trophic factors, controls the properties of muscle fibers. Here I describe how these two discoveries were made, the unexpected difficulties of reproducing the first discovery, and the controversies that followed the second discovery. I discuss why the first discovery took many years to become generally recognized, whereas the second caused an immediate sensation and entered textbooks and major reviews but is now largely forgotten. In the long run, discovering a new phenomenon has greater impact than falsifying a popular hypothesis.

Keywords long-term potentiation (/keyword/Long-term+Potentiation), LTP (/keyword/LTP), synapse (/keyword/Synapse), muscle (/keyword/Muscle), plasticity (/keyword/Plasticity), impulse patterns (/keyword/Impulse+Patterns), neurotrophic factors (/keyword/Neurotrophic+Factors), science history (/keyword/Science+History) Autobiography (/keyword/Autobiography)

INTRODUCTION How are scientific discoveries made? In my case, it was by chance, not by pursuit of an idea. I happened to be in the right labs at the right time, presented with experimental preparations hiding secrets ready to be uncovered with the methods at hand. In Oslo, in Per Andersen's lab, the hippocampus stood at the center, its function essentially unknown at the time. I did not search for what the hippocampus does but rather searched for how its different parts operate electrophysiologically. Delivering brief high-frequency stimulus trains to the main input to the hippocampus, the perforant path, I saw for the first time the long-lasting increase in synaptic efficiency that followed, now known as longterm potentiation (LTP) ( 1 ). Was I aware of its significance at the time? Why had Per not made the same observation earlier when doing similar experiments, and why was I later unable to reproduce the result, causing me to abandon LTP research? Below, I present some answers to these questions. In London, working as a postdoc under Ricardo Miledi at the Department of Biophysics, University College London, I started studying nerve-muscle interactions, a specialty of that lab. The dominant idea then was that motor neurons control the phenotype of muscle fibers by means of trophic substances released at neuromuscular junctions independently of nerve impulse activity. But in one experiment Jean Rosenthal and I turned that idea upside down when we showed that chronic stimulation of denervated muscle restored the normal phenotype ( 2 ). As described below, that experiment led me to doubt the existence of putative trophic factors and to spend the next 30 years exploring the role of impulse activity in muscle cell regulation and looking for alternative ways to explain the evidence for neurotrophic control of muscle that so many neuroscientists found compelling. The two discoveries emerged essentially from one experiment each, in which the results stood out in all their clarity far above the noise—to be reaffirmed, of course, but not to be doubted. For lesser discoveries, experiments often need to be done over and over again so that a reproducible pattern emerges from the noise to confirm their validity. But even then, particularly with commonly used significance levels, results may often be spurious. It so happened that I spent a large part of my life in scientific research on problems thought to be important at the time but that are now forgotten and spent only a small part on making a discovery that turned out to have lasting impact. Below, I make an attempt to answer why some discoveries stick whereas others do not.

THE DISCOVERY OF LTP Joining Per Andersen's Laboratory I graduated from medical school in 1961, worked for two and a half years as a doctor, and then joined Per Andersen's lab in Oslo in 1964. Per had just returned from two productive postdoc years with John Eccles in Canberra, Australia, and had started his own lab in Oslo. I already had some research experience. Five years earlier, as a medical student, I had spent a year at the Institute of Physiology in Pisa, Italy, studying single-unit activity in the visual cortexes of awake rabbits ( 3 ). In Oslo, I worked closely with Per in the lab on anesthetized rabbits and cats for a little over a year, learning the electrophysiology of the hippocampus. We then decided it was time that I started my own experiments for a PhD, which in those days was expected to be independent. Accordingly, on days when Per was not using the lab, I started studying frequency potentiation, a phenomenon presenting itself as a marked potentiation of dentate granule cell responses during repetitive stimulation of the perforant path, a major output of the entorhinal cortex, which Per had already described ( 4 ). The Discovery I first saw LTP during those early experiments in 1966. Stimulating the perforant path with trains of stimuli lasting for up to 10 s at frequencies between 10 Hz and 20 Hz, I observed the frequency potentiation described by Per. But I also observed that the potentiation, as tested by single stimuli after the trains, could last for at least several hours. I presented the results at a meeting of the Scandinavian Physiological Society in Turku, Finland, in the summer of 1966 and, in the abstract from that meeting, concluded: “This represents an example of a plastic change in a neuronal chain, expressing itself as a long-lasting increase of the synaptic efficiency. The effect, which may last for hours, is dependent on repeated use of the system” ( 1 ). Were we aware of the significance of this result? In drafts for seminars and reports at the time, I wrote: “If it is correct that the hippocampus is involved in memory function, this is a region where one should expect long lasting changes to occur. The phenomenon may represent a kind of bahnung [opening] of individual synapses and may have relevance to theories of learning.” Clearly, both Per and I saw its relevance to learning and memory, but, surely, we did not anticipate the importance that LTP has today. Per did not then turn his lab into one studying LTP, and I did not follow up my preliminary findings or include them in my PhD thesis completed 3 years later. Nor did I include frequency potentiation. The PhD Thesis Instead, I quickly turned to more elementary operations in the dentate gyrus to better understand both frequency potentiation and its long-term aftereffects. I used primarily paired-pulse stimulation to study input-output functions and the transverse spread of inhibition and excitation along the septo-temporal axis of the dentate gyrus, which led to my thesis in 1969, entitled: “Synaptic Mechanisms and Organization of the Dentate Area of the Hippocampal Formation.” In October 1969, I submitted four papers to Experimental Brain Research and then left for the postdoc in the Department of Biophysics, University College London. The papers were well received but required some changes. The first two papers were then resubmitted and published in 1971 ( 5 , 6 ). The last two papers, however, remained in my files until almost 40 years later, when I merged them into one paper. Including only original data and figures, the paper was then published in Hippocampus ( 7 ). Enter Tim Bliss Tim Bliss did his PhD with Delisle Burns at McGill University in Montreal, Canada. His thesis, submitted in 1967, was entitled “Factors Affecting the Conductivity of Cortical Pathways,” in which single-unit recordings were made in an attempt to determine how synaptic activity affected synaptic strength. When Burns became head of the Division for Neurophysiology at the National Institute for Medical Research at Mill Hill, London, in 1966, Tim joined him there in 1967 to pursue his interests in learning and memory, using undercut slabs of neocortical tissue, a preparation developed by Burns. Tim wrote: “However, the main conclusion I reached after devoting nearly 3 years to this approach was that it was misguided. The preparation was too complex. It was essential to simplify” ( 8 ). While in Montreal Tim had read a paper by Per on the hippocampus, and, realizing that the relative simplicity of hippocampal circuitry made it a much more suitable preparation, he asked Per about coming to Oslo. When Per heard of Tim's interest in learning and memory, Per said, according to Tim: “Then you should come and talk to Terje Lømo, who has found something that will interest you.” Tim came to Per's lab in August 1968 to work with Per on other hippocampal projects ( 9 , 10 ) and with me on LTP until both Tim and I left for London in October 1969. Our very first experiment confirmed my earlier results beyond our wildest expectations, and with our minds now well prepared, we were immensely excited. Initially, we delivered tetanic and subsequent test stimuli through the same electrode. Then we worried that local changes around a tetanizing electrode tip might lower the threshold for action potential generation in surrounding axons and, if so, that the potentiation might simply be due to the recruitment of additional axons. We overcame this potential artifact by exploiting my finding that the perforant path axons pass as if through a bottleneck in the angular bundle before they fan out to innervate the dorsal part of the dentate gyrus in a lamellar manner [for an update on the lamellar hypothesis, see Lømo ( 7 ) and Sloviter & Lømo ( 11 )]. Accordingly, we placed the tetanizing electrode up-front among axons that targeted only medially located granule cells and placed the test electrode several millimeters caudally in the angular bundle among axons that targeted both medially located cells (the experimental pathway) and more lateral ones (the control pathway). The frequency of test stimuli remained unchanged throughout the experiments. Today, both tetanic and test stimuli are often delivered through the same electrode. In studies on hippocampal slices, the test stimulus strength is then sometimes lowered to near threshold for action potential generation (minimal stimulation). Under such conditions, potentiation by axonal recruitment is difficult to exclude rigorously and is usually not controlled for. The Experiments Our experiments were made in the dorsal (septal) part of the dentate gyrus of adult rabbits anesthetized with urethane and chloralose. The electrodes were placed under visual control by removing the overlying neocortex by suction, which exposed the hippocampus. Stimulation of the perforant path evoked monosynaptic field excitatory postsynaptic potentials (EPSPs) in the molecular layer of the dentate gyrus, where perforant path fibers contact the apical dendrites of dentate granule cells. This EPSP increased abruptly following each tetanization, and the increase persisted in many cases for as long as the experiment continued, often many hours. The population spike, representing monosynaptically driven granule cell discharges, was similarly potentiated at decreasing latency. However, the potentiation varied greatly within and between animals. Within animals, single test stimuli evoked population spikes that varied much less in amplitude after the tetanization, consistent with improved efficiency and reliability of transmission. LTP was pronounced in some animals but was weak or absent in others, affecting some parameters of potentiation more than others. Thus, the potentiation of the population spike was sometimes much greater than could be accounted for by the potentiation of the field EPSP, suggesting increased postsynaptic excitability, later described as E-S potentiation. Input-output studies provided indirect evidence of pathway specificity because after tetanization, potentiation occurred only for stimulus intensities below those used for tetanization ( 12 ), suggesting that only tetanized synapses had been potentiated. Tim and I published these results in 1973 ( 13 ), and in 1995 Roger Nicoll ( 14 ) made the following comment: So the question is, Why did this paper start this dramatic field? First of all, it describes all of the basic phenomena of the process of long-term potentiation. These include pathway specificity, saturation, and an increase in the coupling of the synaptic potential to the discharge of the granule cells. Second, there is not a single controversial result in that paper—a very remarkable thing in this field.” The Experiments That Did Not Work In October 1969, Tim and I left Oslo for London. Approximately once a week, I joined Tim at Mill Hill to continue work on LTP in anesthetized rabbits. To our surprise and dismay, we saw little or no LTP and eventually gave up the project. Tim then joined Tony Gardner-Medwin in the Department of Physiology at University College London to look for LTP in unanesthetized rabbits with chronically implanted electrodes. This time, the experiments worked ( 15 ). Clear long-lasting potentiation (several weeks in one rabbit) was observed in many, although not all, rabbits. I returned to Oslo in April 1971. Tony joined me later that year to continue work on LTP. Again, we saw little or no LTP and, after much effort, switched to other projects. Why did the experiments succeed in some cases and fail in others? Why did Per and colleagues, in an article on frequency potentiation, have to write that “after the cessation of the tetanus, a state of increased excitability of the granule cells is observed for several seconds, sometimes for as long as half a minute?” ( 4 ). I can only speculate. In the early successful acute experiments, a local farmer brought the rabbits (which were approximately £5 each) to the lab. Perhaps these rabbits were less stressed than the animals we used later. In chronic experiments, animals are repeatedly handled and are not held fast for injection of anesthetic before induction of LTP. Regardless, all these rabbits must have been stressed before induction of LTP, but to different degrees, depending on their histories, upkeep, and other factors. Stress markedly and consistently suppresses LTP in CA1 of the dorsal hippocampus of a rat ( 16 , 17 ). Both acute stress and chronic stress suppress LTP in the rat dentate gyrus, where the deficit in LTP correlates with learning impairments ( 18 , 19 ). Rabbits appear particularly sensitive to stress, and stress may have been responsible both for our failures and for the striking variability in LTP expression in successful experiments. Leaving the LTP Field I had every intention of continuing to study LTP, but given the difficulties just described, I returned to the nerve-muscle preparation and the project that I had pursued in London with such success ( 2 ) and that appeared much easier to move forward. At approximately the same time, Tim, working with Chris Richard at Mill Hill, failed to demonstrate LTP in slices from the dentate, probably because they did not block tonic inhibition, which later work showed was necessary at these synapses in vitro. More bad luck occurred in 1974, when Graham Goddard, spending a sabbatical year with John O'Keefe, came to Tim at Mill Hill, and the two of them looked for LTP in rats. Again, in the one experiment that Graham and Tim tried, no LTP occurred. Tim then turned to other problems but returned to the field in 1982 with a paper on glutamate release after induction of LTP ( 20 ). Whose Credit? Tim has written that “credit for the discovery of LTP and its publication in abstract form must go to Terje Lømo” (T. Bliss, personal communication). He then asks whether I would have followed up my observations in 1966 had he not come to Oslo in 1968. And I have answered: “Probably not. On my return to Oslo in 1971, would I then have chosen the hippocampus over muscle, with the success in London behind me and without the work that Tim and I did together? Hardly” ( 21 ). But then I may also ask: Would Tim have made the discovery in Oslo or Mill Hill without the background of my thesis and with the problems of finding any LTP, at least in rabbits? There is hardly an obvious yes to this question. So both of us were essential for the appearance of Bliss & Lømo ( 13 ) in 1973. The First 10 Years For 10 years after the 1973 papers ( 13 , 15 ), there were few publications on LTP and much vacillations about its name. After the failures in 1970 and 1971 described above, Douglas & Goddard ( 22 ) in 1975 were the first to redemonstrate LTP in the dentate gyrus of chronic animals, but this time in the rat. They were also the first to use the term long-term, rather than long-lasting, potentiation. Slightly later in 1975, Schwartzkroin & Wester ( 23 ), using the term long-lasting facilitation, described LTP for the first time in vitro in the CA1 of hippocampal slices from the guinea pig, an early popular source. In 1976, Alger & Teyler ( 24 ) reported long-term potentiation in the dentate, CA3, and CA1 in slices from rats, using the acronym LTP for the first time. In 1977, Andersen et al. ( 25 ) provided direct evidence for pathway specificity of LTP in CA1 in slices from guinea pigs, using the term long-lasting potentiation (LLP). In 1978, McNaughton et al. demonstrated for the first time that LTP expression requires coactivation of many afferent inputs (cooperativity or associativity), naming it long-lasting enhancement ( 26 ) [and later long-term enhancement ( 27 )]. LTP then won the day, presumably because it sounds better and comes off the tongue better than do other acronyms. The Reception Most neuroscientists paid little attention to LTP until the mid-1980s. Bernard Katz and other luminaries in neuroscience showed no special interest at a meeting in Varenna, Italy, in 1969, when Tim and I, among other students, were invited to present our results. As late as 1981, LTP was not mentioned in the textbook Principles of Neural Science ( 28 ) or in Alf Brodal's influential monograph Neurological Anatomy in Relation to Clinical Medicine ( 29 ). Exceptions were the authors just mentioned, Gary Lynch ( 30 ), and John Eccles. Eccles, who visited the lab in Oslo in 1968, immediately became very excited and then started referring to our results using as-yet-unpublished figures in one of his books ( 31 ). The results confirmed his ideas about the importance of synaptic plasticity and revealed what he had been looking for in vain in the spinal cord. The field then appeared to explode after several important findings: the discovery of NMDA receptors and their role in postsynaptic LTP induction ( 32 ), the requirement for postsynaptic influx of calcium ( 33 ), and the relevance of LTP for learning and memory in the behaving animal ( 34 ), together with major technical advances. Per Andersen and His Laboratory In the summer of 1970, Knut Skrede, a medical student in Per's lab, visited Tim Bliss and Chris Richards at Mill Hill in London. There, he learned the technique of maintaining and recording from hippocampal slices in vitro and, upon returning to Oslo, made the crucial switch from longitudinal to transverse slices. The discovery of LTP ( 1 , 13 ), the introduction of the transverse hippocampal slice with intact impulse conduction along the trisynaptic circuit ( 35 ), and the first demonstration of LTP in slices ( 23 ) were all made in Per's lab but, to the surprise of many today, without Per as coauthor. It was the custom for lab leaders then, in Oslo as in the Department of Biophysics in London that I joined later, not to coauthor work they had not directly participated in. There was less competition then and less need for credit to secure future funds or salaries or to be first (or last) in the list of authors, as illustrated by the practice of listing coauthors in alphabetical order in the Journal of Physiology and other journals. There was also, I believe, less direction from above, which offered an independence that I liked. Nevertheless, Per's essential role was obvious. Building on anatomical demonstrations in Oslo of layered inputs in the hippocampus, Per advanced the use of field potential analysis in his PhD thesis ( 36 , 37 ). He introduced Eccles and his lab to this technique in the brain in 1962, and then introduced it to me and then to Tim and many others who came to his lab after 1964. Many also came to work on slices for which Per had developed a chamber that was adopted by many labs around the world. Per set the scene on which all of us could pursue our interests and ideas. The Hippocampus: An Enigma 40 Years Ago As late as 1981, very little was known about the functions of the hippocampus, as the following citations from Alf Brodal's book ( 29 ) show. On page 686, Brodal cites Weisskrantz (from a meeting in 1978): “The striking aspect of the hippocampus is the anatomical elegance of its structure, [and the] really appalling ignorance about what this elegance means.” On page 685, he cites A.H. Black ( 38 ): “One type of theory suggests that a major function of the hippocampus is to modulate motor control systems directly. The second type of theory suggests that the major function of the hippocampus is to control nonmotor behavioral or psychological processes.” And on page 683, Brodal writes: “The anatomical complexity of the hippocampal formation makes it clear that it will be difficult—and perhaps impossible—ever to define satisfactorily the ‘function’ of the hippocampus or of any other part of the hippocampal formation.” The memory loss suffered by the famous patient H.M. must have been well known to Brodal, but he writes (p. 687): “No final conclusion is as yet possible about the structures in the temporal lobe whose damage results in loss of recent memory.” Brodal cites Horel ( 39 ) for references to papers arguing for the importance of lesions in nonhippocampal parts of the temporal lobe. Although Scoville & Milner ( 40 ) entitled their 1957 paper on H.M. “Loss of Recent Memory after Bilateral Hippocampal Lesions,” the recent autopsy of H.M.'s brain shows that the lesion included the tip of the temporal pole, the uncus, most of the amygdala, the entorhinal cortex, and the anterior (temporal) part of the hippocampus but that much of the posterior hippocampus was spared ( 41 ). Lack of the entorhinal cortex, rather than the hippocampus per se, may therefore have been a major reason for H.M.'s severe loss of declarative memories, supporting the caution that Brodal and others expressed at the time. Is LTP Necessary for Learning and Memory? Tim and I concluded our 1973 paper as follows: “Whether or not the intact animal makes use in real life of a property which has been revealed by synchronous, repetitive volleys to a population of fibers the normal rate and pattern of activity along which are unknown, is another matter.” Many researchers have been skeptical about the role of LTP in learning and memory. One extreme position was that of Lichtman & Sanes, who asked “the alarming question” whether LTP exists and further asked: “Could LTP also be a human construct…in the way that our brains handle primary data…finding something when it is not there…a Mickey Mouse in a peculiar arrangements of clouds?” ( 42 ). Another position is that of Gallistel & Matzel ( 43 ), who “compare the properties of associative learning and memory to the properties of long-term potentiation, concluding that the properties of the latter do not explain the fundamental properties of the former.” And yet, more and more evidence points to LTP, or rather the mechanisms underlying LTP, as necessary for learning and memory, but because LTP is hardly sufficient, LTP cannot by itself explain learning and memory. Recent studies of learning and memory in the behaving animal provide strong evidence that LTP is necessary. For example, natural learning of a conditioned reflex ( 44 ), or a sensory input ( 45 ), leads to synaptic changes in the hippocampus or visual cortex that are indistinguishable from LTP. Furthermore, inhibitors targeting the protein kinase PKM block both natural memory storage and LTP maintenance in relevant brain regions ( 46 , 47 ) for up to months after their induction ( 48 ). Although these results were questioned when both the capacity for memory and LTP were shown to persist in PKM knockouts ( 49 , 50 ), they may be accounted for by compensatory upregulation of a closely related molecule. In experimental animals, natural learning occludes subsequent induction of LTP, and induction of LTP occludes subsequent learning ( 51 – 53 ). In humans, similar occlusions are observed between natural learning and LTP-like potentiation ( 54 , 55 ). Numerous interventions that inhibit LTP induction also inhibit natural learning. Multiple forms of LTP exist in neural circuits; some forms depend on NMDA receptors, and other forms depend on other particular molecules. Therefore, the demonstration that some forms of learning can occur in the absence of NMDA receptors ( 56 ) does not exclude involvement of other forms of LTP. As far as I know, there is no evidence that long-term learning and memory can occur in the absence of LTP. The essence of LTP, as I see it, is to allow new functional neural circuits to form endlessly throughout life so that representations of facts, events, acquired skills, and abstract thoughts can be continually stored and later recalled.

IMPULSE ACTIVITY CONTROLS THE PHENOTYPE OF MUSCLE FIBERS As mentioned above, in October 1969, I moved to London for postdoctoral work with Ricardo Miledi at the Department of Biophysics. Jean Rosenthal arrived from Yale, and for the next year and a half, Jean and I worked together in a small lab down the corridor on the fifth floor of the department. The other labs were, or were soon to be, occupied by, among other postdocs, Bill Betz, Mike Dennis, John Heuser, Dale Purves, Bert Sakmann, and Nick Spitzer. The early 1970s were perhaps the last years that American postdocs would flock to Europe for training. As a project, Ricardo suggested that Jean and I chronically block impulse conduction in the sciatic nerve and then examine the effect on the sensitivity to acetylcholine (ACh) in paralyzed but innervated muscle fibers. The Neurotrophic Hypothesis (1970) Denervation interrupts both evoked muscle impulse activity and the delivery of putative nerve-derived trophic factors to muscle. The neurotrophic hypothesis posited that the supersensitivity to ACh and other changes in muscle fibers after denervation resulted from lack of trophic factors rather than from impulse activity, and the hypothesis therefore predicted that the supersensitivity would not develop in the experiment suggested by Ricardo. In 1937, Sarah Tower made perhaps the first attempt to distinguish between evoked impulse activity and trophic factors in the regulation of muscle properties by isolating the lumbosacral spinal cord in kittens to silence the muscle and compare inactive, innervated muscles with denervated muscles. She wrote: “Therefore, since atrophy is apparently inevitable after denervation, whether the muscle be artificially activated or not, both activity and some other as yet unrecognized trophic agent must operate between nerve and muscle beyond the motor end-plate” ( 57 ). Artificial activation in the citation above referred to work by J.N. Langley on denervated muscle treated with electrical stimulation or passive movements ( 58 , 59 ). More evidence for trophic agents emerged in 1960, when Ricardo reported that ACh supersensitivity appeared around denervated endplates in multiply innervated frog muscle fibers kept active by intact innervation elsewhere on the same muscle fibers and, furthermore, that the ACh supersensitivity started to disappear before evoked impulse activity was observed during nerve regeneration. These findings led him to conclude that “the neural factor which controls the number and spread of acetylcholine receptors in the muscle fiber is independent of nerve impulses” ( 60 , 61 ). In 1961, Johns & Thesleff reported that little or no ACh supersensitivity appeared in muscle fibers inactivated by spinal cord isolation (SI) ( 62 ). But because supersensitivity did appear after neuromuscular transmission block by botulinum toxin (BoTx), Thesleff proposed that spontaneously released ACh could be the trophic agent ( 63 ). Before that, Luco & Eyzaguirre ( 64 ) had reported that when nerves were cut at increasingly longer distances from the muscle, the appearance of ACh supersensitivity and fibrillations was progressively delayed, presumably because the release of trophic factors was correspondingly prolonged. Such findings then led John Eccles to write in The Physiology of Synapses (1964): “[I]t can be stated that the evidence for a trophic influence from nerve onto muscle is conclusive, but it is still uncertain whether it is entirely effected by unique trophic influences or whether in part by the spontaneous emission of quanta of ACh” ( 65 ). In their classic cross-reinnervation experiments in 1960, Buller, Eccles, and Eccles ( 66 ) concluded that the neural influence on muscle speed is not exerted by nerve impulses as such. It is postulated that a substance passes down the axons of slow motoneurones, crosses the neuromuscular junctions and traverses the muscle fibres, transforming them into slow contraction units and maintaining them so. Possibly there is also a substance from fast motoneurones that acts via a comparable pathway to accelerate muscle contraction. In a later paper, Eccles and coworkers mention the possibility of “a specific influence of frequency of motoneuronal discharge,” by causing “vibratory stress of activation at a frequency of about 10/sec, an explanation suggested by Professor A.F. Huxley” ( 67 ). The Experiments Jean and I started to block nerve impulse conduction by injecting diphtheria toxin into the sciatic nerve, which by local demyelination at the site of injection caused paralysis of lower leg muscles, and yet motor nerve terminals appeared normal, and spontaneous ACh release was present. Then in 1970 Robert & Oester ( 68 ) reported blocking impulse conduction in the sciatic nerves of rabbits with silicone cuffs impregnated with a local anesthetic around the nerves. We quickly adopted this technique because it appeared easier to use and the paralysis was immediate rather than variably delayed. However, there were problems. As it turned out, the anesthetic was responsible only for the immediate conduction block. The longer-lasting paralysis was due to nerve compression and local demyelination, requiring a tight fit between nerve and cuff that led to a variable degree of axonal degeneration and hence to denervation, which we wanted to avoid. Nevertheless, irrespective of the type of block, innervated fibers, displaying morphologically intact motor nerve terminals and spontaneous miniature endplate potentials, became as supersensitive to ACh as were the denervated fibers. This result was inconsistent with the neurotrophic hypothesis but, as we quickly realized, did not solve the problem because the block might interfere with the production, transport, or release of the putative trophic factor. The next step was obvious. We had to get rid of the nerve by denervation and to substitute nerve-evoked activity with muscle impulse activity evoked by chronic electrical stimulation through implanted electrodes. After much trial and error, by January 1971, a series of four to five rats had been successfully stimulated for 4–5 days. I remember very well the first experiment: two denervated soleus muscles (SOLs), only one of which had been chronically stimulated, lying side by side in the dish. Moving the pipette for ejection of ACh first along the length of denervated unstimulated fibers, I recorded the usual spread of ACh supersensitivity. But then, and to my great excitement, when I moved the electrodes to the denervated stimulated muscle, the fibers were as insensitive as normal fibers, except for one spot roughly in the middle of each fiber. At these spots, which corresponded to denervated endplates, the sensitivity was as high as at normal neuromuscular junctions, but now there were no spontaneous miniature endplate potentials. In that one experiment, which we confirmed in other experiments in the next few days, the neurotrophic hypothesis appeared turned on its head. With no nerve in the muscle, there was no way that a lack of nerve-derived trophic factors could explain the results. It had to be a lack of evoked muscle impulse activity. These results were then published in 1972 ( 2 ). I returned to Oslo in April 1971, and, being unable to reproduce earlier experiments on LTP as already described, I continued with chronic stimulation of denervated muscles and, with my colleagues, showed that such stimulation also restored other membrane properties to normal ( 69 – 71 ). Furthermore, when we stimulated the denervated slow SOL with patterns that resembled the firing patterns of fast motor neurons and we stimulated the denervated fast extensor digitorum longus (EDL) muscle with patterns that resembled the firing patterns of slow motor neurons, we essentially reproduced the effects of crossreinnnervation ( 72 – 77 ). The Reception Many researchers either did not accept our results or thought of trophic factors as essential but acting in conjunction with evoked impulse activity. Here are some examples of the arguments raised against our work and against the idea that loss of evoked muscle activity, not trophic factors, is responsible for the effects of denervation on muscle. In 1976, Deshpande, Albuquerque, and Guth ( 78 ) concluded that “both the prejunctional nerve membrane and the postjunctional muscle membrane are regulated by a neurohumoral factor.” In addition, they wrote: Furthermore, the experiments using prolonged electrical stimulation [Lømo & Westgaard (1975) (Reference 70 ); Westgaard (1975) (Reference 71 )] can be criticized because they were performed on chronically denervated muscles. The denervated muscle fiber is a cell that has been released from many of its physiological regulatory controls; given our present state of knowledge one cannot use such pathological tissue to make inferences about the role of muscle activity on physiologically normal muscle fibers; this experimental approach appears to us to be inappropriate for the study of trophic nerve function. This critique seemed strange. It is common research practice to remove some unidentified factor and then add a specific, identified factor to see whether it can replace the unidentified one and restore normal function, which is what direct stimulation does. In 1976, Ernst Gutmann wrote of “increasing evidence for the existence of neurotrophic (nonimpulse) mechanisms, especially in nerve-muscle cell relations” ( 79 ). In 1981, Jolesz & Sreter concluded: “There is no evidence that the fast activity pattern plays a significant role in determining fast-twitch muscle properties,” suggesting that our stimulations had damaged the muscles and that new fiber formation explained our results ( 80 ). In 1991, Witzemann et al. wrote that “levels of the -subunit in the entire fiber [a sign of ACh supersensitivity] are reduced by a negative neural factor and possibly also by nerve-induced electrical muscle activity” ( 81 ). In 1994, Alan Grinnell ( 82 ) wrote: Because the direct-stimulation experiments are so convincing, it is tempting to conclude that muscle activity is the only factor responsible for many of the muscle properties changed by denervation or that it is essential to their regulation. However, there is compelling evidence that activity-based effects are superimposed on at least two other mechanisms of trophic regulation. And in 2001, the textbook From Neuron to Brain ( 81 ) as evidence for trophic factors.

) cited Witzemann et al. (

83

Trophic Factors Versus Products of Nerve Degeneration In his 1994 review in Myology, Grinnell discussed the evidence for trophic factors under the following headings: “Stump Length Effects,” “Nerve Breakdown Products,” “Nerve Conduction Block,” “Block of Axonal Transport,” and “Pharmacological Block of Synaptic Transmission” ( 82 ). Why did this evidence appear compelling? An important reason was the observation that blockage of impulse conduction in an otherwise intact nerve initially causes less ACh supersensitivity (and lower levels of other denervation-like changes) than does denervation. Because both interventions block evoked muscle activity at the same time, inactivity alone could not be responsible for the additional effects of denervation. According to the protrophic interpretation, continued release of trophic factors from intact but silent motor nerve terminals was responsible for such additional effects. According to the proactivity interpretation, nerve terminal degeneration and accompanying reactions in the muscle were responsible, as such reactions would boost the response of muscle fibers to inactivity. Alberto Cangiano and I have termed such reactions “products of nerve degeneration.” The identity of such products is unknown but would include products from degenerating axons and nerve terminals, denervated muscle fibers, or activated immune and tissue cells. Support for this idea comes from the observation that denervation elicits proliferation and accumulation of tissue cells, including macrophages, in affected muscles in both the frog and rat ( 84 – 86 ). The response is most pronounced in the junctional region but affects the entire length of the muscle. It is also transient, with maximal signs of cell proliferation after 4 days; cell proliferation levels then subside to control values. Importantly, no such tissue reactions are seen after nerve conduction blocks. Thus, Murray & Robbins ( 86 ) concluded in 1982 that “cell proliferation after denervation is not a response to simple disuse, but rather to a nerve-related or muscle-related mitogen.” The responses of muscle to denervation have similarities to inflammation, and acute inflammation induces marked but transient ACh supersensitivity in innervated muscle fibers, as observed in muscles subjected to surgical traumas or the presence of foreign bodies or degenerating nerves on their surfaces ( 69 , 87 , 88 ). However, not only inflammation but also any of the products of nerve degeneration mentioned above could induce ACh supersensitivity and other muscle fiber changes. For the proactivity interpretation to be correct, the greater muscle response to cutting axons compared with that of just blocking their impulse conduction should be transient, like the mitogenic effects of denervation on the muscle. In a series of papers, Cangiano's lab produced what I take as compelling evidence that this is the case ( 89 – 92 ). Thus, denervation markedly speeds up and potentiates muscle fiber responses to inactivity by factors that act only during the first 1–2 weeks of denervation. After that, as convincingly shown by Cangiano, there is no difference between the effects of nerve impulse conduction block and the effects of denervation. Moreover, when a nerve with impulse conduction completely blocked by tetrodotoxin (TTX) reinnervates a denervated muscle, no reduction in ACh supersensitivity (or appearance of TTX resistance of muscle action potentials) is observed, contradicting the neurotrophic hypothesis. Such results lead to very different interpretations of the types of experiments listed by Grinnell ( 82 ) as compelling evidence for trophic factors. Thus, “stump length effects” occur because nerve degeneration appears earlier when the distal nerve stump is short ( 93 ), not because trophic factors disappear earlier. “Nerve conduction block” is initially less effective than denervation because inflammatory or inflammation-like responses are absent, not because silent nerve terminals continue to release trophic factors. “Products of nerve degeneration” also explain the local supersensitivity observed by Miledi around denervated endplates in multiply innervated frog muscle fibers. “Block of axonal transport” relates to the ACh supersensitivity and other denervation-like changes observed after the application of drugs such as colchicine to the sciatic nerve, effects that were attributed to blockage of axonal transport of trophic factors ( 94 , 95 ). However, as Cangiano and I showed independently ( 96 , 97 ), colchicine acts systemically, affecting innervated muscles in different parts of the body equally, regardless of the injection site. In addition, I showed that colchicine affects innervated and denervated stimulated muscle fibers equally, indicating that it probably affects muscle directly and certainly by mechanisms independent of the nerve ( 97 ). “Pharmacological block of synaptic transmission” covers experiments that use TTX, BoTx, and bungarotoxin (BuTx) to inactivate muscle by blocking nerve impulse conduction, transmitter release, and binding of ACh to ACh receptors, respectively. Grinnell ( 82 ) reported from the literature that ACh supersensitivity is highest after denervation, intermediate after BoTx, and lowest after TTX at certain times after onset of treatment. But such experiments are difficult to interpret. The TTX block is only transiently less effective than denervation, and prolonged complete blocks by TTX are difficult to obtain and require special precautions ( 89 , 92 ). Moreover, both BoTx and BuTx are foreign proteins that may elicit inflammation. For example, in the 1991 experiments by Witzemann et al. ( 81 ) (see above), the effects of TTX were lower than expected, suggesting incomplete conduction block, whereas the effects of BoTx were surprisingly large, perhaps because it was injected directly into the muscle and caused an inflammation that enhanced the effects of inactivity. Undetected residual impulse activity in the TTX experiments and inflammation in the BoTx experiments, rather than lack of trophic factors, may therefore have led to the results of Witzemann et al. ( 81 ). Trophic Interactions as Understood Today The neurotrophic hypothesis discussed here postulated nerve-derived factors acting anterogradely onto entire muscle fibers. The factors were trophic (nutritional) in the sense that, in their absence, muscle fibers would atrophy and eventually disappear. Today, lacking support and presence in recent literature, the hypothesis appears discarded. But motor nerve terminals do release other substances with other essential functions; for example, neural agrin, which sets up the postsynaptic apparatus, causes its differentiation and separation from the extrajunctional membrane and elicits the expression of postsynaptic factors that signal back to regulate the differentiation of presynaptic terminals ( 98 ). But because neural agrin affects only the junction, it is not a trophic factor in the original sense. In the peripheral nervous system, the demonstration of nerve growth factor (NGF) in target tissues that act back to promote the survival and maintenance of sensory neurons and sympathetic neurons has led to a generally accepted neurotrophic theory based on retrograde signaling ( 99 , 100 ). Motor neurons also depend on their target (muscle) for their survival, but unique trophic factors have been difficult to demonstrate because different subpopulations of motor neurons respond differently to many candidate factors ( 101 , 102 ). In the brain, both presynaptic nerve terminals and postsynaptic dendrites appear to secrete brain-derived neurotrophic factor (BDNF) in activity-dependent manners ( 103 , 104 ) with effects that may be local in its regulation of synaptic efficiency at particular dendritic sites or more general in its regulation of protein synthesis and neurite and dendritic growth. Secreted from pre- and postsynaptic sites, BDNF may act both anterogradely and retrogradely. Stimulating Innervated Versus Denervated Muscle It is also important to distinguish between the effects of stimulating denervated muscles directly and those of stimulating innervated muscles indirectly via intact motor axons. Much work has shown that indirect stimulation can markedly affect the contractile properties of muscle ( 105 – 107 ). However, this approach does not resolve the issue of trophic factor versus evoked impulse activity because with intact motor neurons it is impossible to rule out an effect of stimulation on the production, transport, composition, or release of putative trophic factors. Moreover, because the self-generated impulse activity of the intact motor neurons is not recorded, the precise pattern of impulses imposed on the muscle is unknown. Advantages of Stimulating Denervated Muscles For many years, my lab was one of few labs that performed chronic stimulation of denervated muscle. Using this approach, we could exclude nerve-derived trophic influences and obtain complete control of the stimulus patterns imposed on the muscle. I believe we were the first to study systematically the role of different impulse patterns in regulating the properties of postsynaptic cells. By varying the frequency and number of stimuli as well as the duration and timing of individual stimulus trains, we described how different stimulus patterns affected not only the rate of disappearance of ACh supersensitivity ( 69 , 70 ), but also the speed of contraction of muscles and their expression patterns of myosin heavy chain and fiber types, as well as many other muscle properties ( 72 – 77 ). Because the slow SOL and the fast EDL responded in strikingly different ways to identical stimulus patterns, we introduced the concept of adaptive range, which posits that patterns of impulse activity regulate the contractile properties of muscle fibers in a graded manner within different intrinsic limits in different types of muscle fibers ( 73 ). By mixing fast and slow stimulus patterns, we obtained intermediate contractile speeds, consistent with graded regulation of and interactions between intracellular pathways toward slow or fast muscles ( 73 ). We showed that a given number of stimulus trains spread over 24 h strongly suppressed ACh supersensitivity, whereas the same number delivered for 6 h every 24 h had only a weak effect ( 70 ), explaining why fibrillatory activity, which is similarly cyclical, has negligible effects on ACh supersensitivity ( 108 ). Such results indicated that reactions to muscle inactivity, such as ACh supersensitivity, occur whenever a single period of inactivity exceeds a certain critical duration. Provided that activity is inserted at shorter intervals, even small amounts can preserve the muscle, as in normal fast motor units ( 109 ). Such findings question the validity of SI for studies of nerve-muscle trophic interactions. For example, according to Edgerton and coworkers, SI “maintains motor neuron-muscle connectivity and thus appears to be a useful model of pure inactivity or disuse” ( 110 ). They report results that “demonstrate a neural effect independent of electrical activity that 1) helps preserve muscle mass, 2) regulates muscle-specific genes, and 3) potentially spares the satellite cell pool in inactive muscles” ( 111 ). However, they also report “occasional movement in the hindlimbs of SI rats during bladder expression” ( 111 ) and record “some action potentials, 1% of the normal total activity, after either SI or denervation” ( 112 ). In view of our results described above, such residual activity is a more likely explanation for the different effects of SI and denervation than any putative activity-independent trophic factor. Our experimental model has been important in identifying activity-dependent intracellular pathways for the control of gene expression. For example, slow, but not fast, impulse patterns trigger the entry of transcription factors, such as the calcineurin-dependent NFAT factors, into the nucleus; these transcription factors then induce a slow phenotype ( 113 , 114 ). In the brain, the decisive role of patterns of nerve impulses in driving synapses toward LTP or long-term depression is today taken for granted. Clinical Applications In 1985 we wrote that “an essential neurotrophic control mechanism seems unlikely in the rat. If this conclusion can be extended to humans, then it should be possible to maintain and perhaps make some use of denervated muscles in humans by suitable electrical stimulation. If, on the other hand, neurotrophic substances are essential, such prospects seem less likely” ( 115 ). Since then, much effort has been made by researchers in Vienna to develop apparatuses and methods for percutaneous long-term stimulation of denervated leg muscles in humans with complete and irreversible lower motor neuron destruction ( 116 – 118 ). After 2 years of stimulation, remarkable improvements are observed in muscle mass, fiber diameter, ultrastructure, tissue composition, and muscle force, with some parameters reaching normal values and 25% of patients able to perform stimulation-assisted stand-up exercises. Stimulations starting after longer delays (>4 years) are much less effective. Patients use home-based stimulators for daily stimulations of gluteus, thigh, and lower leg muscles on both sides. Stimulus durations are initially very long (100–300 ms), but as recovery proceeds, the duration can be substantially reduced to allow for tetanic stimulations of up to 25 Hz for better effects. Limitations are obvious. With no hope of reinnervation and little control of muscle contractions for most useful movements, major benefits for patients are described as cosmetic and entailing improved comfort while they are sitting down due to increased muscle mass. Stimulation-induced muscle contractions and increases in muscle mass, like exercise, may also have long-term health benefits. Concerns may be raised with regard to how many patients will persevere with such demanding, long-term, and (I presume) expensive treatment, particularly with an absence of dedicated experimentalists to follow each patient closely over long periods of time. Nevertheless, the effects obtained are remarkably large, providing evidence that in humans, as in rats, nerve-evoked muscle impulse activity rather than a putative trophic factor is the essential regulator of (nonjunctional) muscle properties. Summing Up Direct stimulation of denervated muscles with appropriate stimulation patterns prevents the appearance of abnormal nonjunctional muscle fiber properties. Hence, there is no need to postulate additional trophic factors. For every type of evidence taken to support the existence of trophic factors, there are alternative and much more plausible explanations that are entirely consistent with a unique role of nerve-evoked muscle impulse activity in regulating nonjunctional muscle properties. Despite much effort, no one has yet identified any factor that can fulfill the roles of putative neurotrophic factors. On the contrary, when factors have been isolated from neural tissue, they induce ACh sensitivity rather than suppress it ( 119 ), as required by the neurotrophic hypothesis. Whereas reports favoring the existence of neurotrophic factors were numerous before 2000, they have now essentially disappeared from the literature, suggesting that the hypothesis is no longer tenable. The search for anterograde trophic factors started with attempts to explain why muscle fibers after denervation become supersensitive to ACh along their length. A mechanism for transporting the factor to the target (i.e., axonal transport) was known. But there was no known mechanism for bringing the factor, or signals induced by it, to each end of the muscle fiber, affecting the entire fiber equally, and the search for such a mechanism came to nothing. In contrast, the conduction of all-or-nothing, nerve-evoked muscle impulses along the fibers did provide a mechanism for affecting muscle fibers equally along their length. The search for retrograde trophic factors began with the attempt to explain why, during development, neurons die after their axons are cut. In this case, a mechanism for bringing the factors from the target to the cell body (retrograde axonal transport) was there. The search led to the discovery of NGF and other trophic factors, and a different type of trophic theory was firmly established.

THE RECEPTION AND LONG-TERM IMPACT OF THE TWO DISCOVERIES It is interesting to compare the long-term impacts of the two discoveries described above and how they were received at the time. Tim and I published the first systematic study of LTP in 1973 ( 13 ), but then many years passed before most neuroscientists became interested. We described a phenomenon, its existence was later confirmed in many laboratories, no one invested in contrary views, and no one disputed the results. In contrast, the 1972 Lømo & Rosenthal ( 2 ) paper caused an immediate sensation. The issues involved were well known, most neuroscientists immediately saw their implications, and the results were quickly included in textbooks and numerous review papers. But because many researchers had invested time, effort, and prestige in sustaining the neurotrophic hypothesis, years of controversies followed our contrary results, until all interest petered out when, despite much effort, no direct evidence for the postulated trophic factor could be found. The differences in the two discoveries bear on prematurity and falsification in science. According to Gunther Stent, “A discovery is premature if its implications cannot be connected by a series of simple logical steps to canonical, or generally accepted, knowledge” ( 120 ). Undoing the neurotrophic hypothesis by direct stimulation of denervated muscle raised no question of prematurity because “everybody” immediately saw its implications. Instead, it is an example of the role of falsification in science. As Karl Popper wrote, “[S]cientific theories, if they are not falsified, forever remain hypothesis or conjectures” ( 121 ). As described above, one experiment falsified the generally accepted hypothesis that neurotrophic factors, acting independently of impulse activity, controlled the properties of muscle fibers. The follow-up hypothesis that both trophic factors and impulse activity are essential is harder to refute. To prove that something does not exist is notoriously difficult. Therefore, to say that nerve-derived trophic factors cannot under any circumstances exert essential control over some muscle property remains conjectural. The discovery of LTP was also not premature, as some scientists immediately saw its implications. Why then did most scientists take little notice? Some possibilities come to mind. First, there was a preference at the time to explore neural mechanisms in simpler preparations from organisms such as squids, Aplysia, crustacea, nematodes, and frogs, in which basic processes common to all neural tissue could be studied in ways that were then impossible in the brain of higher organisms. Second, there was a view of the mammalian brain as too complex, rather unchangeable, and resistant to repair, leading neuroscientists to stay with the simpler preparations, particularly as these continued to yield highly interesting results. Third, there was a certain pessimism about the prospects of fully understanding the brain. “Was progress coming to an end,” as Stent ( 122 ) argued, because of “intrinsic limits of human understanding,” “the brain incapable of providing an explanation of itself”? Brodal ( 29 ) also expressed such pessimism when he suggested “it will be difficult—and perhaps impossible—ever to define satisfactorily the ‘function’ of the hippocampus.” Fourth, insufficient knowledge, inadequate techniques, and too unreliable experimental preparations prevented most people from jumping in. There was also the opinion that ineffective promotion of one's own ideas might delay recognition (see Reference 120 ). In my more optimistic view, it is more a question of methods and new technologies than a question of any inherent limitations, as discussed by Stent ( 122 ) regarding structuralism. As new methods appear and open new vistas of the brain, still newer discoveries and methods are made in an unending process that may well resolve problems thought to be insoluble. It is not uncommon that popular hypotheses fail and disappear from the literature. The idea that multiple types of sensory receptors rather than specific nociceptors generate impulse patterns that lead to pain (pattern theory, gate control theory) is one example ( 123 – 125 ). Medicine is full of failed ideas, as indicated by the many surgical or pharmacological interventions that were abandoned when it became clear that the side effects far outweighed any benefits or that the benefits turned out to be placebo effects ( 126 ). The placebo effect is an example of an idea that was generally dismissed before it became established as a real and important biological phenomenon ( 127 ). Lamarck's hypothesis of inheritance of acquired characteristics, which “everybody” thought of as failed, may have to be partially reconsidered, with epigenetics emerging as a major research field. In other cases, competing hypotheses may create controversies until it turns out that both may be true depending on the situation, as in the debates about electrical or chemical synaptic transmission, presynaptic or postsynaptic expression of LTP, and partial (kiss and run) or complete vesicular exocytosis. In our search for truth, the imperfections of all men and women inevitably come in, as we get carried away by ideas that do not fit the real world, the complexity of this world being underappreciated, and the merits of one's own ideas exaggerated.

CONCLUSION Discovering a new phenomenon has greater impact in the long run than discovering that something previously held to be true is wrong. The first type of discovery leads, as in the case of LTP, to further work and to new insights and discoveries. The second type, as in the case of the trophic hypothesis, may involve a large body of work by believers and nonbelievers alike but will eventually fall by the wayside and be forgotten. Both types of discoveries have impacts as they change the direction of research, but only one of them will stick in the minds of subsequent generations of scientists. DISCLOSURE STATEMENT The author is not aware of any affiliations, memberships, funding, or financial holdings that might be perceived as affecting the objectivity of this review. ACKNOWLEDGMENTS I thank Tim Bliss, Alberto Cangiano, Alan Grinnell, Jack McMahan, Roger Nicoll, Todd Sacktor, Stefano Schiaffino, and Wesley Thompson for very helpful comments during the preparation of this article. LITERATURE CITED 1.

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