The underlying rationale for basic epilepsy research can vary considerably from investigator to investigator. Particularly in trying to attract capable young researchers to the field, it is worthwhile examining – and advertising – the potential attractions of epilepsy research. Similarly, there are many valuable basic research approaches, from exploration and discovery to hypothesis-testing to invention and technological advancement, that may yield important insights and new treatments. Prioritizing research goals, choosing technical/methodological approaches, and identifying useful model systems are all key features of the research experience. Careful consideration of these aspects of the basic research process will, hopefully, optimize productivity and enhance rewards.
This volume and its predecessors1–3 focus on “basic mechanisms” of the epilepsies. Most of us, when we open such a volume, expect to see a discussion of studies on experimental animal models and/or “reduced” brain preparations (i.e., not studies in humans), with an emphasis on cellular, molecular, and genetic variables that influence neuronal excitability, synaptic interactions, and circuitry dynamics. These studies are, typically, carried out in a laboratory, often by individuals who employ some “basic” research skills that are quite different from taking care of patients with a neurological disorder. We “basic scientists” are trained in exacting research techniques, use highly specialized methods, and employ critical faculties that help us avoid the potential pitfalls of experimental approaches.
These features of “basic” research often separate the associated laboratory activities from research carried out on patients with medical disorders – so-called “clinical” research. As we all know, the separation between “basic” and “clinical” is not always easy to make. Physician-scientists may move easily from the laboratory to the clinic, and blur the distinctions. Highly technical approaches developed in the laboratory may be applied to patient populations – and technical advances developed for clinical assessments may eventually be applied in the laboratory. And cellular, molecular, and genetic variables that once were investigated primarily (or exclusively) in animals and in vitro preparations are now routinely applied to clinical populations. Indeed, many of the “basic” imaging and genetic insights into neurological disorders were identified initially in “clinical” studies.
Given how blurred this “basic/clinical” distinction is, it has become increasingly important for basic scientists to break down the basic-clinical separation, and particularly to give up the idea that clinical research is somehow inferior - lacking, perhaps, the rigor or the insights associated with laboratory work. There is, however, an important aspect of research that often (not always) separates basic from clinical studies – the availability of “normal” control groups. One of the major advantages of laboratory work – aside from enabling the researcher to apply “invasive” approaches that would not be ethically appropriate in human subjects – is the possibility of separating variables of interest and therefore creating control groups that differ in only the variable of interest. This laboratory advantage provides the basic scientist with an especially powerful (but narrow) means of drawing strong conclusions from his/her work. It is important to recognize, however, that depending on the goal of the study, isolation of single variables may not provide “answers” that are of clinical value, since the real-life pathologies rarely appear to be dependent on single variables.
WHAT DO WE MEAN BY “BASIC” RESEARCH?
Basic research can take a number of different pathways in the attempt to provide insights and advances. The “basic research” enterprise can be divided into at least three somewhat different activities, each of which involves different approaches and different goals:
Exploration and discovery
Historically and conceptually, “scientific research” begins with exploration, an attempt to see what’s out there. Exploration has not always been respected as a scientific research activity, especially since it may be poorly focused - or “biased” so that the explorer finds what he is looking for. Yet, modern research is almost inconceivable without the “exploration” of a Galileo, of a Darwin. Indeed, where would today’s disciplines of molecular genetics be without the “exploratory” research that resulted in the description of the human genome?
In years past, a grant review that included a phrase such as “this is an exploratory study” or “this is a purely descriptive study” was an inevitable death-knell. We have more recently begun to appreciate the importance of exploratory studies, and to understand that exploration can be pursued on many different levels (e.g., within a large animal population, or within the DNA components of the genome). We seem now to “allow” exploratory research if it is sufficiently molecular (i.e., if the study uses sophisticated modern molecular/genetic tools), but still reject such studies if they use more “ordinary” approaches (e.g., macroscopic or even microscopic observation). Is there a good rationale for accepting descriptive studies at one level, but not at another? Why reject detailed descriptive studies (or label them as second-rate science) if such studies provide a basis for asking important questions?
Hypothesis-testing
Scientific training usually emphasizes the need for well-designed experiments, experiments that typically involve the development of clear hypotheses that can be tested using established (or newly-developed) scientific methods. Key features of this type of research include: a) asking questions (posing hypotheses) that can be “definitively” addressed in the laboratory; b) applying appropriate control/comparison groups; c) replicating the results of the study; d) analyzing the results with appropriate statistical tests; and e) being careful not to over-interpret the data. We are all taught that, in the laboratory, hypotheses can never be “proved,” only disproved. We are taught that experimental data can be used to “support” a hypothesis. We are cautioned against making the jump from one well-controlled experimental context to a general statement of “truth.” Thus, this type of research is carried out in a very narrow and specialized context – and yet it is now the gold-standard for what we think of as good science. Why should that be the case?
Hypothesis-testing is a means by which one can use the results of exploration and discovery (i.e., observations and descriptions) to make predictions about our world. A hypothesis often reads “If …., then ….” That is, given a certain initial condition and/or manipulation, one can reasonably expect a given outcome. “Prediction” is, indeed, the basis for much of scientific research, and has been the driving force underlying the development of scientific method and techniques. Providing a reliable basis for prediction is the job of the researcher.
Invention and technological advancement
Inventors have been among our most illustrious scientists, but modern invention – with its association with financial gain – has been viewed often as a non-scientific function (or at least a less-than-respectable scientific activity). Inventors have been looked at as “tinkerers” or “engineers” – but not as true researchers. Yet, technological invention drives modern science, and the findings from “basic” laboratory (and clinical) research drive technical innovation. Why, then, would one want to separate the technological enterprise from research (either exploratory or hypothesis-testing)? It is often the technological advance that is the ultimate goal of even the most basic forms of research.
WHAT CAN WE ACCOMPLISH BY ENGAGING IN BASIC RESEARCH?
Even if we know what we’re doing, it is often not so clear why we should be doing it. Why would a bright young student want to spend his or her lifetime doing research in the laboratory? What rewards await the researcher? What value does this activity have for our society? The answers to these questions are often assumed by teachers and students, by researchers and granting agencies, by grant applicants and reviewers. But these questions are not simple. Indeed, at least at the general level, the answers may vary dramatically from individual to individual, from discipline to discipline, and from generation to generation.
Knowledge for the sake of knowledge
At every point in history, in every civilization, there have always been individuals who are inherently curious about their environment, who inevitably ask “why” and “how” questions. In modern society, for those who just “want to know,” there is no better way to pursue that goal than in the laboratory. In this sense, scientific research is the modern “religion.” The young research scientist is provided with powerful tools, introduced to complex and intriguing questions, and encouraged to attack difficult problems as a challenge (for the sake of obtaining an answer). While some young scientists enter the field with specific practical goals in mind, most are simply intrigued by the opportunity to study something “cool,” to become good at what they do – and eventually, to be recognized for their expertise and contributions. Obtaining knowledge for its own sake is an old and sacred pursuit, one that is respected (implicitly) in the philosophy of many granting agencies that have very practical agendas. Accordingly, since it is impossible to know how a given discovery or insight might be used (in a practical way) in the future, we should encourage and support even that research that doesn’t seem to offer any immediate application or offer any obvious relevance to real issues and problems. Because of the uncertainty about what insights might become important in the future, because what seems irrelevant or unusable at one time might provide the basis for important future developments, “basic research” without specific practical rationale should be encouraged and supported. This position is certainly not universally held – and it represents a somewhat fragile rationale for basic research in an environment in which resources are scarce.
Control
Inasmuch as research studies allow us to make more and more accurate predictions, they provide us with better and better control over our environment. With an understanding of how things work (i.e., “If…, then….”) comes the opportunity to develop more effective interventions and means for exploiting these mechanisms. Exploratory research provides a starting point for such developments; for example, the description of the human genome has opened up important possibilities for treating – and even curing – many diseases. However, real control (e.g., effective treatments) depends on an understanding of basic mechanisms (e.g., on those processes that connect genetic structure with behavioral phenotype) – which in turn comes as the result of hypothesis-testing research.
One can, to be sure, rely on serendipitous data to obtain “control” of one’s world. For example, many effective medical treatments have been “discovered” without an understanding of underlying mechanisms of the disease. Given this history, there is an ongoing debate about the relative efficacy of research strategies that depend on insights into basic mechanisms. This debate is an important one within the context of epilepsy research. Regardless of the strategy, however, the key rationale for basic research is that the chosen approach will improve our ability to predict outcomes – and to intervene to alter those outcomes.
Quality of life
This capability of effective intervention leads, in theory, to a better quality of life – whether more effective energy generation, better methods for dealing with climate change, or development of improved drugs/treatments that make us healthier and help us live longer. While it may not always have been the case that research could affect the quality of life of the average citizen, public support for research is certainly now based on this assumption. We, as scientists, should be aware of this assumption, which brings with it a social responsibility that perhaps did not exist in the past. The research scientist can no longer think of himself as an isolated agent. As scientists, our goals (as well as our approaches) are shaped by the inter-relatedness and interdependence of research laboratories, and by our ties and obligations to the supporting society. We do not really have a choice about whether our research should be geared toward making improvements for our society. Such a goal is now an obligatory aspect of the research enterprise.
WHY DO BASIC EPILEPSY RESEARCH?
How does all of this general philosophical musing relate to our specific discipline, epilepsy research? In particular, what justifications can we give – to ourselves, each other, and the society that supports us – for pursuing this line of work? The “usual” rationale involves some reference to the identification of better treatments and cures. If that’s the case, then we should be prepared to point to specific accomplishments in our history that show how basic research has led to a better quality of life for people with epilepsy. Indeed, in today’s world, our answers to these questions need to be not only theoretically satisfying (and “correct”) but also practical. If one accepts our obligation, as scientists, to contribute to the society that supports us, then the “Because ...” response must reflect a feasible activity and achievable goals.
Because ... it’s interesting
There’s no getting around the fact that many young researchers are attracted to epilepsy research simply because the problems are intellectually fascinating, the phenomena are dramatic, and the potential experimental approaches allow/encourage the use of a broad array of technical weaponry. There are few neurological phenomena as dramatic as a seizure – whether you monitor it behaviorally, electrophysiologically, or molecularly. Further, there is a broad range of still-unexplored, but very important questions that beckon enticingly to the ambitious young scientist anxious to make his/her own mark in a complex field. In recruiting young investigators, and in discussing the advances in our field with the public, we need to take advantage of the inherent drama of epilepsy, of its complex nature, even of the beauty of so many different systems interacting to produce a clinically-important disorder. In short, the old stigma associated with epilepsy can (and should) be turned on its head to reveal a scientifically compelling mystery.
Because ... it sheds light on general brain function
For better or worse, one could make the argument that basic epilepsy research has shed more light on normal brain function than on the underlying bases of seizures (and their treatments) (e.g., see 4, 5). Because seizure-related phenomena appear to “use” normal brain mechanisms, but involve a dramatic exaggeration of these processes, it is sometimes easier to see what’s going on in the epileptic brain. Nowhere is this relationship more obvious than in the general area of “brain plasticity.” Synaptic modification (e.g., as in kindling6), anatomical reorganization (e.g., sprouting7), and changes in gene expression associated with seizure activity8 have shed light on normal plasticities associated with development, learning and memory, and aging. This interplay between normal and pathologic was evident early in studies using “strychnine neuronography” to map out functional connections in the brain (e.g., see 9) and “Jacksonian march” of epileptic activity to determine the topography of brain motor areas (as explored by Jasper among others – see 10). Epilepsy patients subjected to split brain procedures have given investigators the opportunity to further explore brain localization of function (e.g., see 11), and imaging techniques developed to localize seizure onset zones have been refined to explore higher brain processes (e.g., see 12). Cellular mechanisms so importantly associated with normal brain function – such as soma/dendritic calcium flux,13 regulation of extracellular potassium by astrocytes,14 and recurrent excitation15 – were studied early (and in some cases first identified) in seizure models in which these processes were exaggerated. Research approaches can be honed and investigative tools optimized in studies of seizure phenomenology, so as to gain the sensitivity needed for studying more subtle changes in normal brain function.
In many epilepsies, the brain functions “normally” most of the time. Since a variety of research protocols – including invasive procedures – can be justified to study the epilepsy in those brains (because they are “epileptic”), it may be possible to gain insight into normal brain function by examining the “baseline” state. A clear understanding of the normal neurological baseline is absolutely critical if we are to test theories of epileptogenesis (i.e., how the brain changes from its normal state to the epileptic state); hypotheses focusing on aberrations of normal brain development,16 reversion of the mature brain to an immature state,17 loss of homeostatic controls,18 and uncontrolled “plastic” processes19 all implicitly demand that we define normal brain function which is “pathologic” in the epileptic state.
Not only do epilepsy studies shed light on normal brain function, they also often have considerable relevance for understanding other neurological disorders. For example, epilepsy research now includes studies of mechanisms key to neurodegenerative disorders (e.g., mechanisms of cell damage/death,20 traumatic brain injury (e.g., post-injury reorganization,21 and gene-related change (loss or increase) in function22). The overlap is apparent not only at the laboratory level but also clinically, where it is now clear that “epilepsy” can/should be viewed as a syndrome that often includes important “co-morbidities” beyond the seizure itself (e.g., see 23,24).
Because ... it offers real opportunities for research career development
In modern biomedical research, an investigator’s choice of a research focus is molded not only by his interests, but also by opportunities for making a significant impact and for obtaining long-term funding for one’s research activities. One can, of course, argue about whether basic epilepsy research has been “adequately” funded (relative to other neurological disorders? relative to other conditions that affect such a large percentage of the population? relative to the impact of the epileptic condition on medical costs/spending?). In the U.S., the National Institutes of Health and many private funding agencies provide significant research support, not only for the well-established investigator with a track record of productivity, but also for young investigators (presumably with fresh ideas). And relevant support is available in somewhat unexpected places if one looks (e.g., from the Department of Defense). Despite these funding opportunities, it often appears that the field has lost, or failed to attract and maintain, many high quality researchers; these individuals have chosen to focus their work in other research areas, presumably because they see more opportunity to participate at the “cutting edge” of biomedical research or because they view disease-related research to be “second-class” (compared to “pure” basic research). One of the major challenges to the epilepsy field is to lure outstanding young investigators into this area of research – and retain them for the long-term. Success in this effort will be determined by how well we can “sell” epilepsy as an exciting field of opportunity.
What features of a basic research program are likely to attract top-quality investigators? A list of such features is likely to include the following: 1) interesting problems that have research-based solutions; 2) opportunities to learn and apply modern technologies; 3) activities that involve links/collaborations with outstanding researchers in related fields; 4) high-profile publication opportunities that will gain the respect of colleagues and thus enhance one’s career; and 5) potential for making contributions to a significant health/societal issue. In the epilepsy research field, we have generally relied upon the intrinsic interest of the “problem” – and done relatively little to present relevant research opportunities in a way that explicitly targets these goals. Indeed, until recently we have been rather “fuzzy” about the research challenges that energize our research efforts, and have not been effective in presenting them in a way that is understandable and intriguing to an investigator who is not already committed to this area of research. For example: How many would-be researchers have any idea about the prevalence, varieties, and neurological consequences of clinical seizure disorders? Do we simply want to suppress seizure activity – and if that is our goal, haven’t we already “solved” the problem with available antiepileptic drugs? What are the long-term opportunities and challenges in the field, and how are they related to general neuroscience (or other neurological disorders) research?
Because ... it may lead to development of better treatments and cures
However an epilepsy researcher might start out (whatever the feature that first attracts her to this field), sooner or later she is likely to realize that her laboratory activities actually could have significant consequences for people with seizure disorders. The realization that one’s work in the laboratory could (should?) provide the bases for new treatments (and even cures) is a potent motivator. Given that motivation, a particularly exciting feature about the current state of epilepsy research is the proximity of the laboratory to the clinic. While that potential has always existed in theory (the epilepsy field has always implicitly involved “translational” research), it has never been so “real” as it is today. Modern neuroscience offers the tools and the concepts that can link, in a direct and impactful manner, laboratory insights with clinical practice/treatment. Enhancing that relationship, by encouraging interactions between basic and clinical researchers, provides a strong answer to the question of “Why do basic epilepsy research?”
HOW DO WE CHOOSE AND PRIORITIZE RESEARCH GOALS?
It is all fine and good to make a theoretical commitment to epilepsy research – but what does that commitment really mean? What are the strategies for pursuing meaningful research goals in our field? There are many ways of approaching the challenge, many directions and means for generating meaningful data. Rather than (or in addition to) encouraging a search for “the silver bullet” treatment/cure, it is important to recognize the diversity inherent in “the problem,” and the need for many different hypotheses and approaches. Researchers may find themselves considering the following issues as they determine how they will choose and pursue their experimental goals:
Identification of important problems
In a field as diverse and complex as epilepsy research, search for “the” critical research questions can be a daunting task. Further, the focus of research tends to shift from decade to decade (indeed, year to year) – a normal result of changes that arise as our research tools and conceptual understanding change and become more powerful. In the recent past, as a result of evolving techniques in molecular genetics and of our growing appreciation of the “social” impact of epileptic disorders, there has been an emphasis on such issues as genetic causes of the epilepsies, the involvement of molecular pathways recruited during seizure activity, and the cognitive alterations associated with seizures (or brain conditions that give rise to seizures). In recent publications devoted to an exploration of current and future research priorities, there has been a shift in our research focus to exploring underlying bases of epileptogenesis (mechanisms and treatments), to examining brain development and catastrophic epilepsies (aberrant processes during brain development that lead to difficult-to-control epilepsies and to associated long-term cognitive deterioration), to studying co-morbidities associated with seizure conditions, and to developing new therapeutic strategies (new targets for antiepileptic drugs, and non-drug treatment/cure strategies).25, 26 The shift in focus is driven, at least in part, by new insights at the clinical level, as well as by an appreciation for what can be productively investigated in the laboratory. And the new strategies and targets are made possible by insights and achievements with respect to previous research targets.27 Given the rich complexity of the field, there is no reason to think that there will not be new sets of research priorities when the next Jasper’s Basic Mechanisms of the Epilepsies volume is published.
Understanding basic mechanisms vs. empirical testing
The research issues that call for our research attention can be attacked in what appear to be two fundamentally different ways. On the one hand, investigators can seek the underlying bases of a seizure-related phenomenon. The rationale for this approach seems obvious: If we understand the underlying mechanism, we can design an appropriate intervention/treatment. On the other hand, investigators may choose to test various treatment strategies without knowledge of underlying mechanisms. This approach has been historically quite productive; for example, the identification of most current antiepileptic drugs (AEDs) was carried out without an understanding of their potential mechanisms of action. There is a strong tendency in the current research environment to give priority to the first approach – even though there remains considerable disagreement about the feasibility of, for example, “rationale drug therapy” based on pharmacological mechanisms.28, 29 Part of the problem, of course, is that although we may understand the potential molecular targets of a given drug, we don’t understand (in most cases) the underlying abnormality that gives rise to the epileptic condition. An additional difficulty is that most treatments (pharmacologic and non-pharmacologic) have multiple effects, and it is difficult to determine which action is the antiepileptic one. Does that matter? Should the fact that we don’t understand, for example, the anticonvulsant basis of deep brain stimulation or vagus nerve stimulation lead to a discriminatory bias against (or delay in) using such treatments? Some may argue that most of our current antiepileptic treatments (whether pharmacologic, surgical, or otherwise) have come out of empirical clinical experiences, not from laboratory research and insights into basic mechanisms. The value of elucidating underlying mechanisms is rarely contested. But there is a basic research tendency to dismiss empirical clinical studies as “bad science.” This point of view may have a discouraging effect on the development of novel treatments.
Detailed analyses vs. big picture
A related dichotomy that tends to divide research strategies in different laboratories is whether to seek detailed mechanistic analysis of a narrow variable or whether to invest one’s resources in gathering data that will yield a descriptive picture of a broader nature. Obviously, these two approaches are not mutually exclusive, and most research involves aspects of both approaches. A given laboratory (or researcher) will tend to emphasize one over the other, but will operate somewhere in the middle of this continuum. Interestingly, in most Ph.D. programs, we work hard to train young investigators to focus narrowly on a well-defined problem, to generate a fine-grained analysis of a narrow research target. This “mechanistic” approach has obvious strengths – offering would-be researchers an opportunity to make a significant mark in the field and thus establish a reputation. This approach suffers, however, from the danger of producing rather “myopic” researchers, who don’t really understand the broader context in which they work. It is also clear that what one laboratory sees as “mechanistic” may be simply “descriptive” to another researcher. Finally, given that mechanistic analysis is dependent on accurate description as a first step, and given that most clinically-relevant problems in the epilepsy field are complex and involve multiple variables, careful descriptive studies are critical. Critique of a research program as unacceptably descriptive or irrelevantly narrow ignores the important question of if/how such studies might contribute to an important research goal.
WHAT APPROACHES – CONCEPTUAL OR TECHNICAL – ARE LIKELY TO YIELD SIGNIFICANT RESULTS?
All research – and in particular, all basic epilepsy research – is not created equal. One’s goals will determine, in large measure, how one approaches the problem(s) of interest and the techniques/methods that will most effectively move the study forward. While this point seems obvious, it is not so easy to realize in practice. Indeed, it is often the case that an investigator’s methodological expertise will largely determine the types of experiments that are carried out in his laboratory – and thus limit the investigator’s ability to address the “real” goals of his research. While a single investigator cannot be expected to have such sufficiently broad expertise as to allow his laboratory to choose the most appropriate methodological approaches to a problem of interest, we can expect – and should urge – that the methods and experimental design employed to address a research problem are consistent with the investigator’s stated goals. In the epilepsy field, one might also argue that those goals should provide insights into mechanisms, behaviors, and treatments of epilepsy as a real clinical target.
Conceptual goals
As is the case in any field, the conceptual goal(s) of the basic epilepsy researcher should ideally be well-focused, clearly-articulated, and of significance. As journal editor and grant reviewer, I routinely ask why the author/applicant has chosen to carry out the experiments described in her manuscript or grant application. If I can’t answer that question, then I rapidly lose interest. Because epilepsy is a complex set of disorders, because it is common, and because it has many connections to normal brain function, it is sometimes difficult for an investigator to articulate a clear rationale for her work – not only for the reader (or reviewer) but also for herself. Why is it important to be focused and clear in one’s goals? There are a number of ways to answer that question. Clear research goals lead to: 1) well-designed experimental protocols; 2) less confusion in choosing what variables to study and what experimental models to use; and 3) a baseline from which one can discuss the significance of the research. Confusion about what one can conclude from an experimental study is a common result of insufficient clarity with respect to one’s experimental goals. Conceptual “fuzziness” in basic epilepsy research often involves such confusions as: 1) identifying a cellular/molecular feature in epileptic brain and concluding that – simply because it’s there – it contributes to the epileptic (or epileptogenic) process; 2) assuming that some abnormality described in an animal model of epilepsy (or in an in vitro/reduced preparation) is a feature of a human clinical condition (or responsible for the development or expression of the epilepsy); 3) drawing conclusions about epilepsy (or the epileptic brain) based on findings associated with seizures in a normal brain. Establishing clear experimental goals, and drawing appropriate and well-supported conclusions from experimental data, are not always easy – especially since there may be significant considerations that limit what one can actually study. While such methodological limitations are a fact of experimental life, there is no such restriction on elaboration of one’s conceptual goals.
Technical approaches
As mentioned above, technology (and methodology) often limits what we can study, and technical capabilities of a given laboratory often determine what that laboratory actually does study. Collaborative interactions enlarge a given investigator’s experimental scope. But the investigator is constantly challenged to be sure that the methods and techniques offer an appropriate approach to the problem of interest. Laboratory techniques seem to come in and out of fashion, and there has been a tendency for research directions to change as a function of the availability of new technologies. The investigator must therefore make decisions about if/how to change the direction of his research, based not only on whether a given technique has the appropriate power to address his experimental question but also on whether it is currently “fashionable.” Grant and manuscript reviewers are unquestionably biased in favor of studies that employ “state-of-the-art” technologies, and may question the value of research based on “old fashion” approaches. For example, advances in molecular/genetic techniques give us a new capability for assessing phenomenology and mechanisms at these levels – but molecular/genetic studies do not always provide “better” answers to all questions. Identifying a gene associated with a certain type of epilepsy does not tell us how that epilepsy occurs or how it should be treated; gene discovery is, in fact, only the start of an investigation to answer those questions. Similarly, gene array studies that show changes in gene expression in epileptic brain provide only a starting point. These studies do tell us that the epileptic brain is “different” from normal brain – but we know that. The real issue is to dissect out the differences that are critical to (causal of) the epileptic (or epileptogenic) condition. That is not to say that we should not take advantage of new technologies. There is no question that modern technologies have provided the researcher with previously unheard of opportunities for addressing questions that might provide significant insights into important questions. These technologies and methods should certainly be adopted into our arsenal of research tools. But in doing so, investigators need to remain aware that these techniques do not make it any easier to ask, or answer, the “right” questions.
Model development
Among the many challenges and opportunities faced by the basic epilepsy researcher is the often bewildering proliferation of “models.” The investigator almost invariably will need to determine which model(s) best addresses his experimental goals, a determination that includes asking such questions as: What is this a model of? What questions can be effectively addressed? What laboratory techniques are compatible with studying this model? What variables and end-points can be measured? Depending on one’s research goals, some experimenters may not need to work with an animal/tissue model at all (i.e., the investigation can focus on the “real” thing – epilepsy in the human patient30 – or can employ computer modeling approaches31). One must ask also: What should be modeled? To find out what? How? Why? These questions have been addressed in some detail in the recent volume Models of seizures and epilepsy and so the following discussion will summarize only key points that are directly relevant to the general question of “Why do basic epilepsy research?”
Because it’s interesting and fundable (provides opportunities for career development)
As indicated above, there are many features of the epileptic brain that are attractive because of their general relevance to normal brain function and/or to other neurological disorders, and/or because of the ease with which they can be approached with modern techniques. The choice of appropriate models for this type of research can be overwhelming. Investigators routinely use in vitro preparations of single neurons (or neuron-like cells) and glia to study function of channels, receptors, intracellular messenger systems, protein trafficking, etc. – all with the rationale that alterations in the function of these variables can give rise – in some way, at some point in a complex process – to the abnormal electrical activity that defines seizures. Some critics have disputed whether such “reduced” preparations are accurately labeled “epileptic” (or whether individual neurons can produce “epileptiform activities” or “seizures”). It is nevertheless certainly worthwhile to study the underlying bases of aberrant cellular development and activity on their own merits. And arguably, this type of information will provide insights into epileptic phenomenology that could not be obtained from more complex systems. Simplified preparations also often allow for the application of powerful genetic, molecular, and electrophysiological methods that are difficult to employ in complex models. A striking example of successful pursuit of an epilepsy-relevant problem, using molecular genetic insights applied at the cellular level, is the recent identification of the mTOR pathway in tuberous sclerosis.34 Analysis of many epilepsy-relevant mechanisms is facilitated by “reduced” preparation models, but often requires a more complex system of synaptically interacting neurons (or neurons and glia) as provided in acute slice and organotypic culture preparations (e.g., modulation of tonic inhibition35). Because of the methodological sophistication often associated with studies on reduced preparations, these models are often seen as particularly attractive when applying for research support. Many investigators have developed successful and productive epilepsy research careers based on a focus on simplified preparations, and there is a temptation to assume that these models are somehow superior to more complex models (because they are amenable to complex manipulations, one can control and study a small number of variables, etc.). We need constant reminding about the limitations involved in interpreting data from such experiments with respect to our goal of “explaining” epilepsy phenomena or elucidating epilepsy mechanisms. For example, to study the interactions between neurons and endogenous inflammatory molecules requires a system that includes immune system elements.36 Similarly, recent interest in the role of the blood-brain barrier37 or of hormonal modulation of epileptogenicity38 requires models in which those elements are present and normally functional.
Seizures are inherently interesting as a dramatic neurological “output,” and many laboratory manipulations can induce seizure-like phenomena. It is not always clear, however, that all of these experimentally-induced seizure-like activities have anything to do with “epilepsy.” In past years, much of the basic research focus in epilepsy laboratories has been on models in which seizure-like electrical activities (or molecular changes) are induced in an otherwise normal brain. While we now know that seizure discharge in the “normal” brain may be different from output from an epileptic brain, the ease of inducing such activities and the strong attraction to the seizure output per se have encouraged studies in “normal” tissue. There is no doubt that many of these investigations have provided important insights into potential epileptic (and epileptogenic) mechanisms. But investigators who choose to focus on these types of models (i.e., in which seizure phenomenology is induced in normal brain tissue) should be aware, at the outset, that these studies may be of primarily intrinsic interest, since the results may not be relevant to “clinical” epilepsy phenomena.
Because it sheds light on how the brain works
Many investigators have, over the years, argued that epilepsy provides a unique opportunity to understand normal brain function. For example, the key role of calcium – so much the key to research on synaptic plasticity and excitotoxicity – was an early focus of epilepsy researchers studying neurons that produce epileptiform “burst” discharge.39, 40 Co-morbidities associated with epilepsy have begun to receive more attention, and investigators can now look to a large list of epilepsy models to study, for example, cognitive deficits, psychiatric abnormalities, and aberrations in brain development (e.g., see 41). Investigations in animal models of seizure-related anxiety, depression, and other mood/psychiatric disorders38, 42, 43 parallel the clinical focus on these co-morbidities.23, 44 Historically, lesions that have been associated with temporal lobe epilepsy have also led to a greater understanding of memory mechanisms,45 of cognitive decline associated with neurodegenerative disorders such as Alzheimer’s disease,46 and neurogenesis.47 It is important to realize, in approaching studies of brain function through the use of epilepsy models, that it is critical to place such studies into a relevant theoretical framework in order to make any sense of experimental results. The observation of seizures in an animal model of Alzheimer’s disease doesn’t necessarily tell you anything about epilepsy or about Alzheimer’s disease. But if approached within a framework that links seizure mechanisms and Alzheimer’s-related neurodegeneration and/or circuitry reorganization, such observations may provide the basis for interesting and insightful investigation.
Because it can lead to better treatments and cures for a common (and disabling) neurological disorder
It has been historically very difficult to “model” human epilepsy in animals, and investigators have developed a variety of strategies for making findings from animal models “relevant” to the human disorder. Most commonly, the implicit approach has been to choose some feature of epilepsy (or, more accurately, one of the many different types of epilepsies) to study in detail. For example, many basic research investigations have employed models of temporal lobe epilepsy, examining such features as mossy fiber sprouting,7 changes in inhibition in various hippocampal brain regions,48, 49 recurrent excitation,50 etc. This approach provides a host of research possibilities, offering many different methodological approaches. One can look at genetic, molecular, electrophysiological, pathological, and behavioral variables. One can study seizure events, interictal activities, post-ictal behaviors, or even phenomena not apparently linked to a seizure but which occur in the brain of an epileptic individual. The investigator can “make” the relevant phenomenon experimentally (e.g., by injecting a drug) or look at phenomena that occur “spontaneously” in a model system (e.g., a genetically epileptic mouse).
There is a long and still-ongoing argument about how completely a model of epilepsy should recapture the key features of the human clinical disorder in order to be considered a “relevant” model. This argument has had no winner. Ideally, a “relevant” animal model should exhibit spontaneous seizure discharges that resemble – behaviorally/clinically/electrically – the seizure type(s) of interest. Such a high criterion may be unrealistic, however, when one considers how different the human brain is from a rodent brain (in which most such models are developed), the differences in developmental maturation and aging, and the difficulties in assessing seizure expression in non-human subjects. Particularly if the epilepsy type is complex, holding out for such a “relevant” model may impede research rather than encourage it (see 51 for an interesting discussion about modeling infantile spasms). Alternatively, many investigators have turned to rodent models in which the key defining feature is a gene mutation that parallels a clinically-occurring genetic mutation in humans. In these models, one can certainly make the case for the genetic “cause” of the epilepsy – but not necessarily for the relevance of subsequent gene expression. A number of drug treatments (and other experimental interventions) also give rise, over the long term, to spontaneous seizures, often associated with the pathological features that resemble those seen in human epilepsy (e.g., hippocampal sclerosis, as seen in temporal lobe epilepsy52, 53).
The decision to use one of these models should certainly be based on the question the investigator wants to answer. For example, a genetic model may provide important insight into the molecular pathways that determine brain epileptogenicity (e.g., in models of cortical dysplasia). But is such a model “relevant” if one is to use it to study/understand the cognitive dysfunction seen in epileptic brain? Is the time-frame of seizure onset important (e.g., how well does the rodent recapitulate the human maturational sequence with respect to the mechanism under study)? If one uses such models to examine, for example, seizure-related changes in gene expression, can one successfully dissociate expression changes associated with seizure activity from expression patterns that characterize epileptogenicity (i.e., the seizure-sensitive state) or epileptogenesis (i.e., the development of the seizure-sensitive state) – or an underlying brain lesion? One might choose a genetic model based on its clinically relevant neuropathological characteristics, as opposed to a model that mimics seizures discharge/electrical excitability. The long-term functional consequences of the associated structural abnormality, with respect to epileptogenicity or cognitive co-morbidity, may be explored in such a model, even if the animal is not spontaneously “epileptic.” Under what conditions would such a model be “relevant”? Whatever approach one takes, it is important that the choices be made on the basis of a coherent theoretical framework.
Modern epilepsy research has yielded a “new” set of variables that appear to be characteristic of epileptic brain, ranging from high levels of neurogenesis to robust expression of immune system variables to subtle changes in baseline tonic inhibition.36, 54, 55 That these changes are seen in epileptic tissue seems clear. The saliency of these phenomena for epileptogenesis and/or seizure activity remains to be established. Further, as is often the case in research, the more we learn, the less clear are our assumptions about epilepsy mechanisms. For example, it is becoming increasingly clear many (most?) epileptic conditions are not easily attributable to a single genetic/molecular/electrophysiological abnormality, but are reflections of multiple changes – each one often subtle – that together give rise to aberrant brain activities. Thus, the models we choose must eventually provide us with the possibility of exploring the interaction among contributing variables. “Two-hit” hypotheses have become fashionable when thinking about developmental insults that give rise to seizure activities,56, 57 and provide examples of how models may be manipulated to explore multi-factorial contributions to the epileptic state.
Much of the research focusing on basic mechanisms of the epilepsies has revolved around identifying new treatment options – whether involving new drugs or focusing on novel therapeutic strategies. Both strategies can be pursued in a plethora of models. A major concern in these studies is whether the treatment efficacy must be assessed against spontaneously-occurring seizure activity in an epileptic animal, or whether some other measure of excitability (or synchrony) would provide an equally useful assessment. The verdict is still out, and investigators are looking for appropriate epilepsy-related phenomena – “biomarkers” – against which they can measure the effects of their treatments (e.g., a stable frequency of spontaneous seizures58; fast ripples59). In drug studies, it is important to understand also the relative concentration effects (absorption, BBB penetrations, uptake into parenchyma, etc.) in humans (and particularly epileptic humans) compared to the chosen animal model, and at different developmental ages. Since many animal models involve a “normal” brain in which seizures are generated, the question of if/how such neural tissue compares to “epileptic” tissue with respect to pharmacokinetic and pharmacodynamic issues must be addressed.
CONCLUDING THOUGHTS
There are multiple factors that go into the decision to carry out basic research, and additional influences that will determine whether an investigator decides to devote a lifetime of work to studying epilepsy-related issues. The motivation for these decisions, and the subsequent choices that must be made about what problems to tackle and what techniques to employ, often play out in the absence of conscious attention. Just as it is important to give careful consideration to the choice of laboratory techniques or animal models, so too is it helpful to be aware of the factors influencing one’s research directions. As indicated above, there are no “correct” choices to be made. What is important is that the choices be consistent, coherent, and defensible.
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