Three examples of pathways from science to health benefits

The first, and in many ways the best known, example is provided by the effects of smoking on a range of adverse health outcomes such as lung cancer and coronary artery disease (RCP, 2004; Office of the US Surgeon General, 2004, 2006). The story starts with Doll & Hill's (Reference Doll and Hill1950, Reference Doll and Hill1954) case-control observational study showing a huge difference between cases and controls with respect to smoking. Note that the starting point here did not come from any kind of basic science, but rather from an observational epidemiological study. At first, there were attempts to explain away the finding on the basis of a genetic liability (Fisher, Reference Fisher1958a, Reference Fisherb) or in terms of other confounding variables. However, over the years it became clear that the effects of confounders would have to be huge to account for the case-control differences; also the finding that health risks diminished when individuals stopped smoking increased the probability of a causal inference. By the early 1960s, both the Royal College of Physicians (RCP) in the UK and the Surgeon General in the USA published separate reports that identified smoking as a likely cause of lung cancer.

Nevertheless, doubts continued to be expressed. The epidemiological findings led on to laboratory studies with animals that showed the carcinogenic effects of the tars present in cigarette smoke. Much more recently, effects on gene expression were demonstrated (see Academy of Medical Sciences, 2007). By 2004 it had become very clear that the causal inference was so strongly supported from multiple research strategies that public health actions were indicated. In the past few years, too, evidence (once again spanning epidemiological studies and animal experiments) showed the effects of passive smoking. The causal inferences appear well supported, although the health risks are much lower than those with active exposure. The consequence is that in many countries bans on smoking in public have now been introduced.

Several lessons may be drawn from the smoking story. First, this was an example in which the starting point did not come from basic science but, instead, epidemiological findings prompted the need for animal models and for studies of gene expression that took the matter further. Second, randomized controlled trials (RCTs) were clearly not feasible and, hence, causation had to be tested in humans using observational data. That meant that rigorous crucial studies seriously considering non-causal interpretations were essential, and these were carried out. Third, the health benefits from eliminating smoking mainly had implications at a population level rather than at a patient treatment level. In other words, health benefits need to be viewed in public health terms as much as in individual patient treatment terms (see also Rose, Reference Rose1992). Fourth, it took some 50 years to proceed down the pathway from the original findings to health benefit actions. Fifth, the progress came through a combination of research strategies that involved an iterative interplay between observational studies and basic science and back again (Academy of Medical Sciences, 2007; see also Kraemer et al. Reference Kraemer, Lowe and Kupfer2005).

The second example concerns the effects of lipids in predisposing to coronary artery disease (Steinberg, Reference Steinberg2004, Reference Steinberg2005a, Reference Steinbergb, Reference Steinberg2006a, Reference Steinbergb). In this case, it could be argued that basic science constituted the starting point in that, as long ago as 1913, it was shown that feeding rabbits very high doses of purified cholesterol in sunflower oil induced vascular lesions closely resembling human atherosclerosis, both grossly and microscopically. Nevertheless, this early research was ignored, partly because rabbits are herbivores with near zero cholesterol intake in ordinary circumstances, partly because the results in rats and dogs were different, but most of all because the findings were inconsistent with the prevailing view of atherosclerosis as an ageing disease. During the 1940s and 1950s, experimental work provided much new information about lipoproteins in the blood, and in 1956 a multi-site longitudinal study showed that lipoprotein levels strongly predicted later cardiac events. These observational findings led to further laboratory studies involving a range of animal species that confirmed the previously rejected rabbit findings.

Despite this growing body of evidence, the lipid hypothesis had very powerful opponents who dismissed the whole idea. Nevertheless, proponents of the lipid hypothesis drew attention to the observational findings with familial hypercholesterolaemia (a monogenic disorder) that showed the crucial link between mutations in a gene influencing lipid levels, and the strong association with atherosclerosis. Ecological studies similarly showed a link between cholesterol levels and coronary deaths, and the large-scale Framingham epidemiological longitudinal study showed the strong risk effect of cholesterol levels on the liability to have a heart attack. Dietary studies showed the benefits of reducing cholesterol intake, but the benefits were small and not very convincing with respect to the causal inference. Scepticism continued.

The situation changed during the 1970s with the immense gains in the understanding of lipoproteins deriving from basic laboratory research. A pathogenic model of how low density lipoprotein (LDL) penetrated the artery wall to give rise to the diagnostic lesion established, for the first time, a clear mechanism for the lipid hypothesis. A coronary primary prevention trial in the 1980s in the USA provided better evidence on the benefits of reducing LDL levels, but it was only with the development of the statins in the 1990s that a series of large-scale RCTs firmly settled the cholesterol controversy. It was not just the use of RCTs but also the availability of drugs that have a very large effect on cholesterol levels that made the difference. The lessons from this story are somewhat similar to those derived from the smoking example. That is to say, the pathway extended over nine decades and progress came in a series of steps bringing together the crucial non-experimental epidemiological evidence, experimental animal studies, genetic evidence, clinical observations, and clinical trial data. It was also important that the basic science provided key evidence on the biological mediation, but it was the non-experimental epidemiological data that prompted basic science, not the other way around. In this case, unlike the smoking story, the main benefits might be viewed in terms of the treatment of individual patients rather than public health considerations, but the latter are crucial in terms of prevention policies. It should be added that, in this example, as with others, the strongest evidence came from studies of extreme groups and there is the ever-present need to undertake studies to determine the extent to which findings can be extrapolated to variations within the normal range.

The third example is provided by the foetal alcohol syndrome (Randall, Reference Randall2001). Although reports of possibly damaging effects on the foetus stemming from mothers' heaving drinking of alcohol in early pregnancy go back very many years, the first postulation of a distinctive syndrome came from the observation by clinicians of a particular pattern of malformations in the offspring of chronic alcoholic mothers (Jones et al. Reference Jones, Smith, Ulleland and Streissguth1973). A distinctive set of facial features was described and it was argued that these reflected damage to the developing brain brought about by the exposure of the foetus to high alcohol levels in early pregnancy. Numerous reports on humans confirmed the observation and also showed that this was accompanied by abnormalities in behavioural development (see Gray & Henderson, Reference Gray and Henderson2006). What seemed to clinch the causal inference was the demonstration in studies of mice that embryos exposed to high doses of alcohol developed cranio-facial malformations closely resembling those seen in the human foetal alcohol syndrome. Subsequently, mouse studies have contributed much more to examine the adverse consequences resulting from foetal exposure to alcohol, and these have also shown strain differences in vulnerability to alcohol exposure, as well as pointers to the likelihood that developmental exposure to alcohol involves epigenetic effects on genetic networks. In this case, it was an observational study by clinicians that provided the starting point and it was these observations that prompted the need for laboratory studies using animal models. Once more, the pathway led from the clinical studies to basic science, rather than the other way round. As with the smoking example, the main implications are health concern public health measures rather than treatment approaches for individual patients. As Insel & Scolnick (Reference Insel and Scolnick2006) noted, the great public health success stories of the past century are largely stories of prevention rather than treatment (see also Hörig et al. Reference Hörig, Marincola and Marincola2005). As we discuss in more detail below, many questions remain and, again, the need is for an iterative approach from clinical science to basic science and back again.

Putting these three examples together, it is clear that it is necessary to reject the notion that the only (or even the main) pathway goes from basic science to patient care. As indicated in the title of Peters' (Reference Peters2004) Harveian Oration, the pathway is as often from clinical research to the laboratory: from the bedside to the bench, rather than the bench to the bedside. The long time-frame is obvious and so are the public health implications, as much as benefits for individual patients. The three examples above also underline the message of Himsworth's (Reference Himsworth1962) Harveian Oration in which, in reviewing the role of the Medical Research Council, he emphasized the falsity of a sharp categorical dichotomy between so-called basic and applied research. He argued that both non-experimental and experimental research were needed to obtain health benefits, and that knowledge needed to flow from practice to research, as well as from research to practice. As we discuss further below, there is also the clear message that many different steps are needed in proceeding along the pathway and that many of these involve hypothesis testing in the field of clinical science, as much as in basic science. This is what is often conceptualized as ‘experimental medicine’.

Experimental medicine that bridges basic and clinical science

It has been argued that the heart of translational research resides in phase I trials, in which novel treatments are tested for feasibility and toxicity in preparation for a phase II trial, in which therapeutic effectiveness is tested (Marincola, Reference Marincola2003). Although we agree on their importance, we disagree that that is the essence of translation. Rather, we suggest that the key feature is a hypothesis-testing approach that investigates mediating mechanisms with respect to either causation or treatment. Often, too, this may involve an iterative approach that takes a human observation between some environmental factor and disease as its starting point, goes on to test for environmental mediation, and then examines possible biological pathways for that mediation, proceeding next to animal models to examine these experimentally, and then returning to the human situation to determine whether the mechanisms apply to human disease. The study of gene–environment interaction in varied branches of medicine provides telling examples (see Rutter, Reference Rutter2008). Often a key methodological step has been the development of a biological measure likely to be involved in the disease process but which, because it reflects a challenge or stress, gives rise to an immediate response without the need to wait years for the disease to develop. For example, the inhalation of CO₂ provided just such a stimulus in the study of panic (Battaglia, Reference Battaglia and Rutter2008); effects on neural structure and function assessed through brain imaging following an acute emotional stimulus did so in relation to depression and also antisocial behaviour (Pezawas et al. Reference Pezawas, Meyer-Lindenberg, Drabant, Verchinski, Munoz, Kolachana, Egan, Mattay, Hariri and Weinberger2005; Meyer-Lindenberg et al. Reference Meyer-Lindenberg, Buckholtz, Kolachana, Hariri, Pezawas, Blasi, Wabnitz, Honea, Verchinski, Callicott, Egan, Mattay and Weinberger2006); autonomic reactivity and salt sensitivity did the same in relation to hypertension (Adamo & Tesson, Reference Adamo, Tesson and Rutter2008). It is clear that, for this sort of research programme to be able to proceed iteratively, there must be not only creative clinical science but also scientists who can themselves span basic and applied research strategies involving both human studies and animal models, or work in collaborative interdisciplinary teams that achieve the same result.

Basic neuroscience (including genetics)

The achievements of basic science with respect to both genetics and neuroscience have been nothing short of awesome during the past half century or so (Andreasen, Reference Andreasen2001; Bloom, Reference Bloom2007; Charney & Nestler, Reference Charney and Nestlerin press). Indeed, the magnitude of the scientific achievements has been recognized in the award of numerous Nobel prizes. With respect to genetics, it could reasonably be claimed that basic science did provide the starting point. The discovery of the helical structure of DNA by Crick and Watson in 1953 opened up a new understanding of how genes might work. This was followed by demonstration that the genetic code was based on a series of three bases (known as codons), by the discovery of how the amino acids provide these codons, by the discovery of the mechanisms involved in the switching off and on of genes and by the mechanisms involved in the copying of genes – to mention but a few examples – all of which led to Nobel prizes. Our understanding of genetics has been totally transformed by these discoveries and the potential for ultimate translation into health benefits is clear. Nevertheless, it has to be said that even this very fast-moving field has not yet got to the stage when there is any straightforward translation into health benefits (other than with a very few examples of Mendelian disorders, such as the dietary treatment of phenylketonuria).

Much the same applies to the research on brain plasticity. The Nobel prize-winning work by Hubel and Wiesel in the early 1960s clearly showed the importance of both sensitive periods and the role of sensory input in programming brain development. At first, the effects were thought to reflect the effects of sensory disuse but it soon became apparent that competition was crucial (Hubel & Wiesel, Reference Hubel and Wiesel2005). Over the 40-plus years since Hubel and Wiesel's early discoveries, there have been numerous confirmations by other investigators, with further animal studies taking the field forward in a host of important ways (Bateson et al. Reference Bateson, Barker, Clutton-Brock, Deb, D'Udine, Foley, Gluckman, Godfrey, Kirkwood, Lahr, McNamara, Metcalfe, Monaghan, Spencer and Sultan2004; Marshall & Fox, Reference Marshall and Fox2006; Nelson & Jeste, Reference Nelson, Jeste, Rutter, Bishop, Pine, Scott, Stevenson, Taylor and Thapar2008). Our understanding of the ways in which experiences play a role in brain development has hugely increased over the years but it is not as yet entirely clear how that understanding may be translated into health benefits. Nevertheless, with respect to both genetics and biological programming, basic science is already leading to advances in knowledge that will undoubtedly be crucial in producing health benefits in the future, possibly sooner than pessimists suggest.

It might be thought that basic science must have played a role in the development of the numerous drugs now being used to treat mental disorders. In fact, however, most of the key drugs came from serendipitous observations by clinicians, rather than basic science discoveries (Ayd & Blackwell, Reference Ayd and Blackwell1970; Basu et al. Reference Basu, Pereira, Aitchison, Stein and Wilkinson2007). It is true that these clinical discoveries prompted some outstanding basic science on drug actions, leading to Nobel prizes for the mode of action of antidepressants, and of drugs used to treat schizophrenia. This provides yet another example in which clinical research led to basic science, rather than the other way around. Despite the much improved understanding of drug actions, numerous questions remain (Volkow & Swanson, Reference Volkow, Swanson, Rutter, Bishop, Pine, Scott, Stevenson, Taylor and Thapar2008). Currently, the greatest needs include the experimental use of imaging techniques and pharmacogenomics to understand drug actions. These should lead to translational studies in the years ahead, but perhaps progress requires advances in pathophysiology as well as on the mechanisms of drug actions. Historically, pharmacology has focused largely on recipes for ‘me-too’ compounds, rather than treatment developments based on knowledge of pathophysiology (see Insel & Scolnick, Reference Insel and Scolnick2006). Neuroscience should, and ultimately will, provide that biological understanding but, despite some promising leads, there is a substantial way to go (Hyman, Reference Hyman2007).

Social neuroscience constitutes another area in which animal studies have been influential through the indication of the role of the amygdala (see, for example, Damasio, Reference Damasio1994; Aggleton, Reference Aggleton2000; Amaral & Corbett, Reference Amaral, Corbett, Bock and Goode2003; Blakemore, Reference Blakemore2008). Claims have been made regarding its potential importance for psychiatry (Marshall & Fox, Reference Marshall and Fox2006; Harrison & Critchley, Reference Harrison and Critchley2007) but it remains to be seen quite how such findings should be translated into health benefits. Up to now, the most extended discussion has concerned the role of the amygdala in the clinical syndrome of psychopathy (Blair et al. Reference Blair, Mitchell and Blair2005; Patrick, Reference Patrick2006), and suggestions that abnormalities in mirror neuron functioning may constitute the basis of autism (Williams et al. Reference Williams, Whiten, Suddendorf and Perrett2001; Rizzolatti & Craighero, Reference Rizzolatti and Craighero2004; Dapretto et al. Reference Dapretto, Davies, Pfeifer, Scott, Sigman, Bookheimer and Lacoboni2006); see below for a fuller discussion of both. The suggestion derives from animal studies showing cells that responded to viewing both actions and implied actions by others (Rizzolatti & Craighero, Reference Rizzolatti and Craighero2004). The implication is that this might constitute the basis of mentalizing skills of a kind that are impaired in autism. Human imaging studies have shown consistently that mentalizing skills activate the medical prefrontal cortex and the posterior superior temporal sulcus (Blakemore, Reference Blakemore2008). The findings are potentially very important but, at present, most of the research involves the bridging ground of experimental clinical studies that seem to link brain imaging findings with cognitive processes, rather than translation into improved clinical care or public health considerations.

Cognitive neuroscience, especially in relation to memory functions, has constituted a major growth area with some very important findings. The study of memory has a long history in psychology, going back to the late nineteenth century. However, it is probably fair to say that the modern concepts of memory began in the 1960s with recognition that a distinction needed to be drawn between short-term and long-term memory (Craik & Lockhart, Reference Craik and Lockhart1972) and between episodic memory and semantic memory, meaning memory for words, facts or information of an objective type, rather than events of a personal kind (Tulving, Reference Tulving1962, Reference Tulving1989, Reference Tulving2002). After that, a crucial stimulus for this research came from the clinical studies of patients in which there was a dissociation between different memory functions. The study by Milner and colleagues (Scoville & Milner, Reference Scoville and Milner1957; Milner et al. Reference Milner, Corkin and Teuber1968) of a patient called HM, who, as a result of a neurosurgical removal of the medial temporal lobe and hippocampus, lost all long-term memory skills but retained both general intelligence and short-term memory and new learning, constituted the challenge that prompted Kandel (Reference Kandel2007) to investigate the molecular mechanisms involved in the consolidation and storage of memories. His creative series of studies on the sea snail Aplysia led to a Nobel prize. Meanwhile, Baddeley (Reference Baddeley1976, Reference Baddeley1986, Reference Basu, Pereira, Aitchison, Stein and Wilkinson2007) and others took up the challenge presented by Craik & Lockhart (Reference Craik and Lockhart1972) to determine how short-term memories came to provide the basis of long-term memory. More recently, functional brain imaging studies (see Frith, Reference Frith2007) have been important in locating the brain areas that were activated by these memory functions. As with some other examples, it was the clinical and human experimental studies that led to the basic science, rather than the other way round. Nevertheless, the basic science was essential in identifying the neural mechanisms involved at the cellular level. Thus, studies of the function of nerve cells in the hippocampus have shown the importance of a mechanism called long-term potentiation (LTP) (Bliss & Lømo, Reference Bliss and Lømo1973; Bliss et al. Reference Bliss, Collingridge and Morris2003). The unravelling of the mysteries of how memories function in terms of the workings of the mind, the localization of these workings in different parts of the brain, and the determination of how all of this happens at the single cell level provides a splendid example of how different types of clinical, experimental and basic science all contributed essential elements in the discovery process (Milner et al. Reference Milner, Squire and Kandel1998). The findings on the molecular basis of memory have been crucial in showing the specificity of processes, opening up the possibility of the development of drugs that may be used selectively either to enhance memory or to block unwanted memory (see Kandel, Reference Kandel2007). In the years ahead, this may well lead to translational studies but the time is not quite there yet.

A further area of basic science, known as epigenetics, has given rise to hugely important implications for mechanisms that regulate gene expression in response to the environment, without modifying DNA sequences (Jaenisch & Bird, Reference Jaenisch and Bird2003; Meaney & Szyf, Reference Meaney and Szyf2005; Rutter, Reference Rutter2006a; Jirtle & Skinner, Reference Jirtle and Skinner2007; Mill & Petronis, Reference Mill and Petronis2007). These are likely to be involved in biological programming (see below). Molecular studies showed the chemical mechanisms within the cell, such as methylation, that are involved in effects on gene expression. Experimental animal studies then took the field further forward through their demonstration that environmental influences affected epigenesis and, by so doing, affected both neuroendocrine and behavioural functioning (Meaney & Szyf, Reference Meaney and Szyf2005). The clinical potential of the findings lay in their demonstration of one possible biological mediator of long-term environmental influences, and of the interdependence of genes and environment. The environment cannot alter gene sequences but it can alter genetic effects through their impact on gene expression. Because the epigenetic status of the genome is tissue specific and developmentally regulated (as well as influenced by stochastic and environmental factors), post-mortem brain investigations constitute a crucial research strategy. Thus, Mill et al. (Reference Mill, Tang, Kaminsky, Khare, Yazdanpanah, Bouchard, Jia, Assadzadeh, Flanagan, Schumacher, Wang and Petronis2008) showed how epigenetic profiling revealed DNA methylation changes associated with schizophrenia and bipolar affective psychosis. There is substantial potential for the identification of epigenetic biomarkers associated with a liability to disease and to its course. Potentially, they could be used in novel preventative and therapeutic approaches. Animal models will be crucial in this process of discovery but translation into the human situation will also be essential. That is where experimental medicine bridging research is needed before moving to drug studies.

There are then two clinical areas where there is, probably, a rather closer relationship between basic science and possible clinical applications. Dementia is the first of these (Jucker et al. Reference Jucker, Beyreuther, Haass, Nitsch and Christen2006). The story began over 100 years ago with the account by Alzheimer of plaques and tangles in the brain of a patient who died at age 56. Over the next half-century there were many other similar accounts but a major impetus was provided by the clinical studies undertaken during the 1950s and 1960s that indicated a clear demarcation between the dementias and the affective and paraphrenic psychoses (Roth, Reference Roth1955). A key paper in 1966 demonstrated for the first time a quantitative association between the severity of dementia and the number of senile plaques found on post-mortem examination (Roth et al. Reference Roth, Tomlinson and Blessed1966). This led to molecular studies of the paired helical filaments found in the tangles (Goedert et al. Reference Goedert, Klug and Crowther2006a, Reference Goedert, Spillantini, Chetti, Crowther, Klug, Jucker, Beyreuther, Haass, Nitsch and Christenb; Spillantini et al. Reference Spillantini, Murrell, Goedert, Farlow, Klug and Ghetti2006). Again, it was an example of where clinical observations led on to basic science. Basic science, however, was crucial in showing the role of tau protein in the filaments, with hyperphosphorylation as the key change, which was responsible not only for Alzheimer disease but also for other neurodegenerative disorders. This was also found to be connected with mutations in the tau gene. Over the same period of time, there was much other research in the field of Alzheimer disease concerned with the role of amyloid.

Roberson et al. (Reference Roberson, Scearce-Levie, Palop, Yan, Cheng, Wu, Gerstein, Yu and Mucke2007) brought some of the key elements together in their study of transgenic mice with a gene concerned with the amyloid precursor protein. The mice showed amyloid plaques but not neurofibrillary tangles. These mice were then given a reduced tau expression (obtained by crossing mice with the mutant amyloid precursor protein with mice in which the tau gene had been inactivated). Strikingly and surprisingly, the reduction in tau prevented the behavioural disturbances, memory loss and sudden death that was usual in the mice with a variant of the amyloid precursor protein. Curiously, however, there were not effects on the accumulation of amyloid plaques. The implication is that tau (like several other neuronal molecules) potentiates the excitotoxic effects of the amyloid precursor protein. Nevertheless, as Ashe (Reference Ashe2007) cautioned, the timing of the reduction in tau may be critical and extrapolation from mice to humans has still to be shown.

Another different approach was taken by Small et al. (Reference Small, Kepe, Ercoli, Siddarth, Bookheimer, Miller, Lavretsky, Burggren, Cole, Vinters, Thompson, Huang, Satyamurthy, Phelps and Barrio2006), who used positron emission tomography (PET) in conjunction with injection of a molecule that binds to plaques and tangles in vitro. Significant group differentiation was found among healthy controls, individuals with mild cognitive impairment and those with Alzheimer's disease. The technique carries the potential to determine regional cerebral patterns of amyloid plaques and tau neurofibrillary tangles in life, and hence to provide a good biomarker. Nevertheless, the overlap between groups was too great for the marker to be used for individual diagnosis without further development. It is obvious that both of these findings carry important clinical implications, but direct translational studies have yet to be undertaken (see below).

The other clinical field is that of drug dependence. Both animal studies and human experimental studies have contributed to providing a better understanding of the mechanisms involved in dependence (Everitt & Robbins, Reference Everitt and Robbins2005; Academy of Medical Sciences, 2008; Heath et al. Reference Heath, Lynskey, Waldron, Rutter, Bishop, Pine, Scott, Stevenson, Taylor and Thapar2008). The problem with extension of genetic findings to clinical work is that most of the research has been concerned with the response to individual drugs, whereas the clinical and epidemiological evidence indicates that most problems of dependence and abuse concern multiple different substances. The situation is changing to some extent with genetic studies of impulsivity and other behaviours in animals that are closer to the clinical phenomena. There is a greater neuroscience base with respect to the extensive evidence of associations between brain features (Everitt & Robbins, Reference Everitt and Robbins2005) and drug use. These are not in serious doubt but sorting out which features are causes and which consequences of drug usage is no easy matter, although important progress is being made (see Academy of Medical Sciences, 2008). The potential for translation will be present but it is uncertain whether that point has arrived at the moment.

One of the key challenges in much of psychopathology concerns the importance of age changes in the onset and course of mental disorder (Rutter et al. Reference Rutter, Maughan and Kim-Cohen2006). Thus it is now well accepted that, although schizophrenia as an overt psychosis does not usually present until late adolescence, the neurodevelopmental risk features are apparent in the preschool years. Accordingly, there is a need to determine the nature of both the early brain features and the transition into overt psychosis in late adolescence/early adult life. It is now clear that there are important brain changes occurring during adolescence (Blakemore, Reference Blakemore2008) and prospective studies of high-risk families have been informative in showing the features associated with the transition into psychosis (Johnstone et al. Reference Johnstone, Ebmeier, Miller, Owens and Lawrie2005). Prospective imaging studies of individuals with early onset schizophrenia (Rapoport et al. Reference Rapoport, Addington and Frangou2005) have shown that there are both brain features that differentiate at onset and changes that follow onset. This example illustrates the potential of top-quality clinical science to take further our understanding of the neural underpinning of the age-related changes.

Animal models have the advantage of being able to study developmental change by using animals with a much shorter age-span than humans, as well as allowing more invasive methods of investigation (see Academy of Medical Sciences, 2007). The animal model of Rett syndrome (Guy et al. Reference Guy, Hendrich, Holmes, Martin and Bird2001) was successful in producing a phenotype that included the crucial age changes seen in humans. Similar issues apply to the study of autism, with its characteristic increase in brain size during the preschool years (i.e. the opposite of that found in Rett; see Courchesne et al. Reference Courchesne, Carper and Akshoomoff2003, Reference Courchesne, Pierce, Schumann, Redcay, Buckwalter, Kennedy and Morgan2007; Redcay & Courchesne, Reference Redcay and Courchesne2005). However, so far there is not a mouse model that reflects this age change.

A rather different example is provided by the apparent age difference in the risks for schizophrenia associated with heavy use of cannabis. The human evidence suggests that the risks apply to heavy use in adolescence but not in adult life. Although this cannot be modelled in mice, age-related cognitive effects of cannabis have been shown (Schneider & Koch, Reference Schneider and Koch2003; Pistis et al. Reference Pistis, Perra, Pillolla, Melis, Muntoni and Gessa2004), and these show the same age difference found in humans.

Numerous other examples could be given (see Rutter et al. Reference Rutter, Maughan and Kim-Cohen2006) and it is clear that neither basic science nor clinical science has adequately taken up the challenge of investigating the biological mechanisms underlying age changes. That constitutes one of the key priorities for future research.

It is evident that, despite the huge strides that have been made and continue to be made in neuroscience, there is little that is at a point at which direct translation into clinical application is feasible. However, there is much that is at a point where hypothesis-driven human studies using an experimental orientation can provide an important bridging function. In the field of mental disorders, this bridging field is most conveniently considered under the broad heading of experimental medicine. In the section that follows, we consider some of the challenges that need to be taken up. If the desired health benefits are to be obtained, there will need to be some changes in both basic science and clinical research. The former will need to take more seriously a consideration of how it might lead to translation. Clinical science will need to pay more attention to leads from basic science, and bridging studies going between the two will need to focus on biological mediating mechanisms. Jumping straight from basic science to RCTs is doomed to expensive failures but real worthwhile benefits can be expected from keeping health benefits firmly in mind. This has to lead to appropriate actions and not just promises.

Nevertheless, any area of science is bound to involve a host of unanswered questions that need to be tackled. The greater our scientific understanding, the greater the likelihood of health benefits. Moreover, in many cases it will not be possible to judge how clinical applications will follow. That is why it is essential to preserve and strengthen high-quality basic science. However, health benefits will not follow automatically unless translational needs are taken seriously.

Challenges for translational research on mental disorders

If we take the example already discussed of the foetal alcohol syndrome, it is evident that there are many unresolved questions of both theoretical and practical importance. For example, it is known that there are prenatal alcohol exposure effects that are not associated with the diagnosable congenital anomalies that define the full foetal alcohol syndrome. There are massive differences in the rate of diagnosis of these partial syndromes in the USA and the UK, differences that highlight the need to undertake systematic research to determine which of these broader phenotypes are, and which are not, due to prenatal alcohol exposure (Gray et al., unpublished observations). Similarly, it remains uncertain whether the effects in both the full and partial syndromes are mainly due to peak alcohol levels (as in binge drinking) or average alcohol levels. Equally, there is the question as to whether the risks, which are known to be maximal in the first trimester, also extend into the second and third trimesters. Is there a safe limit below which there are no alcohol exposure effects? All of these are answerable questions and require clinical science of a type that involves epidemiological studies. Nevertheless, at the moment those questions do not constitute the main focus for either animal models or clinical research. This is exactly the sort of situation in which hypothesis-based clinical science is crucial to provide a bridge between the basic science and health benefits (in this case being concerned as much with population implications as with individual patient care).

As already noted, the discovery, in monkey studies, of mirror neurons constitutes one of the most exciting and potentially important discoveries in the field of social neuroscience. Direct evidence for these neurons in humans is limited, but there is persuasive circumstantial evidence, particularly through the use of transcranial magnetic stimulation and functional brain imaging (Rizzolatti & Craighero, Reference Rizzolatti and Craighero2004). The possible relevance to autism was shown in a functional imaging study of brain responses to the initiation and observation of facial emotional expressions in adolescents with an autism spectrum disorder (ASD), together with a comparison group of typically developing children matched for age and IQ (see Dapretto et al. Reference Dapretto, Davies, Pfeifer, Scott, Sigman, Bookheimer and Lacoboni2006). The two groups differed in degree of activation of the pars opercularis area, shown in monkeys to be rich in mirror neurons. Moreover, in the human ASD group, activation of the pars opercularis was significantly negatively correlated with ASD symptomatology. The way ahead would seem to lie in a further development of experimental approaches to the use of imaging in young children, focusing on imitation, joint attention and theory of mind (Rutter, Reference Rutter, Charney and Nestlerin press).

As we have noted, one of the most exciting recent discoveries in basic science concerns the role of epigenetic mechanisms in modifying gene expression. Laboratory studies established that methylation constituted one of the key processes (although there are other chemical processes as well). Because it was known that environmental factors influenced gene expression, this provided the potential mechanism by which environmental influences might bring about enduring effects. Such effects were particularly likely to apply to biological programming, but they could operate much more widely. A series of experimental studies, using rodents, by Meaney and his colleagues (Champagne et al. Reference Champagne, Chretien, Stevenson, Zhang, Gratton and Meaney2004; Weaver et al. Reference Weaver, Cervoni, Champagne, D'Alessio, Charma, Seckl, Dymov, Szyf and Meaney2004) established through cross-fostering studies that these effects were indeed due to environmental, rather than genetic, influences, and that the mechanism involved DNA methylation. The approach falls into what we have termed bridging studies in that they used the basic findings on methylation but examined their effects in an experimental fashion. The approach is one that, in principle, could equally be applied to humans were it not for the fact that gene expression tends to be both tissue specific and developmental-phase specific. The brain is unusual in having a high proportion of genes expressed (as compared with other body tissues) and it may therefore be the case that gene expression might be indexed, in a rough and ready fashion, by using, say, blood lymphocytes (Tremblay, Reference Tremblayin press). In humans, gene expression can also be examined, using case-control techniques, with post-mortem brain tissues (see above). In addition, epigenetic differences within monozygotic pairs could be studied with respect to possible environmental sources of differences in gene expression, which appear to be important throughout the life course (Fraga et al. Reference Fraga, Ballestar, Paz, Ropero, Setien, Ballestar, Heine-Suner, Cigudosa, Urioste, Benitez, Boix-Chornet, Sanchez-Aguilera, Ling, Carlsson, Poulsen, Vaag, Stephan, Spector, Wu, Plass and Esteller2005). It is obvious that this is quite some way from having immediate direct clinical implications, but epigenesis obviously does have clear clinical relevance. For example, the important phenomenon of resilience (meaning resistance to adversity; Rutter, Reference Rutter2006b) has usually been viewed in terms of psychosocial mechanisms, with an expectation that fostering resilience requires psychosocial interventions. More recently, the research on gene–environment interactions (Caspi & Moffitt, Reference Caspi and Moffitt2006) pointed to the role of genes in affecting environmental responsivity. Epigenetics raises the further possibility of environmental effects on gene expression, with the implication that pharmacological interventions might have a place in countering adversity or promoting resilience (see Rutter, Reference Rutter2006b). The research evidence is not yet at a point when direct translational research would be appropriate, but further bridging studies in humans, seeking to elucidate the effects of environments on gene expression, would take matters much closer to clinical applications.

A related issue concerns the effects of environmental deprivation on biological programming (related because it has been argued that biological programming is mediated by gene expression). By programming, we mean the varied processes by which environmental input shapes brain development (see Rutter, Reference Rutter, Marshall and Fox2006c). Human studies in the UK of children who spent their first few years in extremely depriving Romanian institutions showed remarkably enduring effects extending at least 7½ years after leaving institutional care (Rutter et al. Reference Rutter, Beckett, Castle, Colvert, Kreppner, Mehta, Stevens and Sonuga-Barke2007). An understanding of the mechanisms involved in these persistent effects is crucial for the planning of appropriate interventions, but bridging studies are needed to take that forward. Longitudinal studies have shown that the effects of psychosocial deprivation outweigh the much more minor effects of subnutrition and they have also shown that psychosocial deprivation, even in the absence of subnutrition, has a marked effect on head growth, and by implication brain growth (Sonuga-Barke et al. Reference Sonuga-Barke, Beckett, Kreppner, Castle, Colvert, Stevens, Hawkins and Rutterin press). Curiously, however, the effects of psychological deprivation on head growth were found not to mediate the effects on psychological outcomes. Imaging studies are needed to elucidate the mechanisms further. An alternative approach, followed by Zeanah et al. (Reference Zeanah, Nelson, Fox, Smyke, Marshall, Parker and Koga2003), has been to examine the effects of children removed (as part of an RCT) from institutions to be reared in foster families in Romania (Nelson et al. Reference Nelson, Zeanah, Fox, Marshall, Smyke and Guthrie2007). ERP findings have been used as an index of possible mediating brain changes. The translational element of both the UK and Romania studies has been the focus on the mechanisms involved both in the occurrence of lasting sequelae and in resilience and recovery from profound deprivation. Both sets of studies are now focusing on mediating mechanisms, a key first step in devising appropriate preventive and therapeutic interventions. Approaches of this kind have a much wider applicability with respect to seriously abnormal experiences. It is crucial, however, to use a hypothesis-testing approach in which possible alternative mediating mechanisms are compared with one another. Merely gathering further descriptive data on risk outcomes following seriously adverse experiences will not be sufficient. Translation requires identification of the nature of the biological processes involved in these risk outcomes and in the protective mechanisms that provide resilience in the face of serious adversities.

Genetic research strategies also have a most important place in testing environmental mediation hypotheses (Rutter, Reference Rutter2007b). Far too often, recommendations on policies and practice to deal with the ill-effects of adverse experiences on mental health have assumed environmental mediation of risk. Findings on gene–environment correlations have made clear that this is not always a safe assumption (Plomin & Bergeman, Reference Plomin and Bergeman1991). It is crucial to test the two main alternatives of genetic mediation and of person effects on the environment. Quantitative genetics has proved its value in tackling these possibilities (Kendler & Prescott, Reference Kendler and Prescott2006; Rutter, Reference Rutter2006a). Hypothesis-testing bridging approaches in the spirit of experimental medicine constitute the first step in translation. Thus, for example, using a longitudinal twin study design, Jaffee et al. (Reference Jaffee, Caspi, Moffitt, Polo-Tomas, Price and Taylor2004) showed that although the effects of overt physical abuse on children's psychological functioning was largely environmentally mediated, the same did not apply to corporal punishment. On the contrary, there was a tendency for regular use of corporal punishment to carry with it an increased risk of escalation into overt abuse. The findings provide a neat example of how genetic strategies can take forward an understanding of environmental mechanisms. The implication is that environmentally mediated risk applies to overt abuse and not to corporal punishment but, on the contrary, regular reliance on physical methods of punishment increases the likelihood of leading on to abuse. The implications for translational research into parenting programmes are obvious.

Both quantitative and molecular genetic research has shown the importance of genes in their influence on individual differences in the liability to most forms of mental disorder. It is clear that an understanding of gene effects should provide important leads in the elucidation of the pathophysiology of mental disorders and, hence, of the neural substrate. The challenge for translational research is how to carry forward that potential in a way that leads to health benefits. Alzheimer disease illustrates well both the potential and the difficulties. The strongest genetic association with the non-Mendelian forms of the disease concerns the apolipoprotein E (apoE)-4 allele variant, which is associated with an increased risk and an earlier age of onset by some two decades (Roses et al. Reference Roses, Pericak-Vance, Saunders, Rimoin, Connor, Pyeritz and Korf2005). Despite the strength of the association, it is generally agreed that it should not be used for prediction of the disease in the general population because absence of apoE-4 does not rule it out, nor is it useful in differential diagnosis. Nevertheless, a mouse model showed that apoE-4 is associated with amyloid deposits and neurofibrillary plaques, indicating a causal role.

Initially, most people tended to view apoE-4 as a susceptibility gene for Alzheimer disease. However, two sets of findings meant that this needed to be questioned. To begin with, apoE-4 has been found to be associated with a range of outcomes stemming from brain injury and not just with Alzheimer disease. Accordingly, it could be that the mode of action involves a sensitivity to environmental hazards that impact on the brain, rather than susceptibility to a specific disease process. In addition, there is some indication that it may also be related to variations in normal ageing. Accordingly, the genetic liability may not be disease specific. However, if the nature of the pathologic process could be identified, that should have clinical implications. The problem is that controversy continues on whether the plaques or the neurofibrillary tangles constitute the key causal element, or whether both may be late-stage non-specific consequences of brain degeneration. As a consequence, clinical translation remains some way off. Most effort has (instead of focusing on the neuropathology) concerned the development of drugs to aid memory. This constitutes a most worthwhile endeavour but it does not (as yet) contribute to the prevention of Alzheimer disease. The challenge remains.

Gene–environment interaction (G×E) constitutes a somewhat different pathway from science to health benefits deriving from molecular genetics. In this case, again, basic science provided the technology, but the application of molecular genetics applied it in a hypothesis-testing fashion to investigate the possibility that the genes operated on sensitivity to the environment rather than on disorders as such (Caspi & Moffitt, Reference Caspi and Moffitt2006; Rutter, Reference Rutter2007a). The investigation of G×E raises a range of methodological challenges (Rutter, Reference Rutter2007b; Uher, Reference Uher and Rutter2008; Uher & McGuffin, Reference Uher and McGuffin2008), but the findings appear robust. The potential importance of G×E is that it implies that the causal pathway for genetic influences and that for environmental influences may be the same. The next step, however, requires elucidation of the neural effects of G×E. This is not basic science, but requires hypothesis-testing research of the type that we have labelled experimental medicine. The approach is well exemplified by the experimental studies undertaken by Hariri et al. (Reference Hariri, Mattay, Tessitore, Kolachana, Fera, Goldman, Egan and Weinberger2002, Reference Hariri, Drabant, Munoz, Kolachana, Mattay, Egan and Weinberger2005) and Meyer-Lindenberg et al. (Reference Meyer-Lindenberg, Buckholtz, Kolachana, Hariri, Pezawas, Blasi, Wabnitz, Honea, Verchinski, Callicott, Egan, Mattay and Weinberger2006), using structural and functional imaging. Two very important findings are apparent. First, the G×E was associated with both structural and functional neural effects (indicating how it may operate on brain mechanisms) and, second, the effects apply to individuals without measurable psychopathology (as well as those with a disorder). This means that the G×E applies to an aspect of a dimensionally distributed function in the general population, and not just to the origins of a particular form of mental disorder. These, and other, hypothesis-driven approaches are forcing a reassessment of the possible ways in which genes operate; a reassessment that gets a crucial step nearer to clinical application.

Psychopathy constitutes a very different clinical syndrome that is relevant to translational issues. The clinical identification of a syndrome characterized by deficits in emotional responsiveness occurred more than six decades ago but the potential integration with neuroscience came about much more recently, as a result of two separate sets of findings. First, functional neuroimaging studies showed that individuals with this clinical pattern had a different response in the amygdala from what is usually found (Blair, Reference Blairin press), that is the amygdala playing a key role in emotional processing (Phelps & LeDoux, Reference Phelps and LeDoux2005). That led to the question of what mind processes were associated with the psychopathic failure to respond to other people's distress. Dadds et al. (Reference Dadds, El Masry, Wimalaweera and Guastella2008) found that a key feature was a lack of looking at people's eyes. This raised the further query of whether the emotional deficit could be the target of treatment (Dadds, Reference Daddsin press). Second, quantitative genetic studies showed that psychopathy involved a higher heritability than that found with antisocial behaviour not accompanied by psychopathic features (Viding et al. Reference Viding, Blair, Moffitt and Plomin2005). It remains to be determined how the genetic liability connects with the amygdala findings, and whether this can be translated into clinical interventions. Hypothesis-testing bridging research would seem to be what is most needed.

A more direct translational task derived from genetic findings concerns the role of genetic counselling. Traditionally, such counselling has been provided by medical geneticists who approached the task from the perspective of Mendelian disorders. The issues in relation to multifactorial mental disorders are very different in several respects. First, there is a need to consider broader phenotypes that reflect genetic liability but that are not obviously associated with a major handicapping disorder. This means that the genetic counselling has to involve quite difficult diagnostic issues with respect to milder phenotypes in relatives. Second, the risks are not only probabilistic but also may well be contingent on co-occurring genetic background factors or encountered environmental hazards. Inevitably, that means that the communication task is much more complicated. Among other things, it entails conveying an understanding that a markedly increased relative risk may still mean a very low absolute risk. The translational research needs to involve several different issues. To begin with, there needs to be a study of the communication and understanding of the concepts of risk, and there also needs to be a study of people's response to counselling when this applies to multifactorial disorders. There have been several studies of genetic counselling in relation to Mendelian disorders but very little research in connection with multifactorial disorders. That clearly constitutes a major translational research need.

In this section of the paper, our focus has deliberately been placed mainly on the bridging research that is essential for a successful pathway from science to health benefits. Curiously, despite its central importance (see Peters, Reference Peters2004), it may be most at risk in the ill-considered rush to go straight from laboratory science to RCTs. Of course, there is a crucial place for RCTs, but the supposed dichotomy between so-called basic and applied sciences is artefactual and damaging in overlooking the many steps needed in that pathway, the most fundamental of which involve hypothesis testing outside, as well as inside, the laboratory.