What will the RDoC initiative by NIMH achieve?
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There's a lot wrong with current psychiatric classification. Every few years, the American Psychiatric Association comes up with a new set of labels and diagnostic criteria, but whereas the Diagnostic and Statistical Manual used to be seen as some kind of Bible for psychiatrists, the latest version, DSM5, has been greeted with hostility and derision. The number of diagnostic categories keeps multiplying without any commensurate increase in the evidence base to validate the categories. It has been argued that vested interests from pharmaceutical companies create pressures to medicalise normality so that everyone will sooner or later have a diagnosis (Frances, 2013). And even excluding such conflict of interest, there are concerns that such well-known categories as schizophrenia and depression lack reliability and validity (Kendell & Jablensky, 2003).
In 2013, Tom Insel, Director of the US funding agency, National Institute of Mental Health (NIMH), created a stir with a blogpost in which he criticised the DSM5 and laid out the vision of a new Research Domain Criteria (RDoC) project. This aimed "to transform diagnosis by incorporating genetics, imaging, cognitive science, and other levels of information to lay the foundation for a new classification system."
He drew parallels with physical medicine, where diagnosis is not made purely on the basis of symptoms, but also uses measures of underlying physiological function that help distinguish between conditions and indicate the most appropriate treatment. This, he argued, should be the goal of psychiatry, to go beyond presenting symptoms to underlying causes, reconceptualising disorders in terms of neural systems.
This has, of course, been a goal for many researchers for several years, but Insel expressed frustration at the lack of progress, noting that at present: "We cannot design a system based on biomarkers or cognitive performance because we lack the data". That being the case, he argued, a priority for NIMH should be to create a framework for collecting relevant data. This would entail casting aside conventional psychiatric diagnoses, working with dimensions rather than categories, and establishing links between genetic, neural and behavioural levels of description.
This represents a massive shift in research funding strategy, and some are uneasy about it. Nobody, as far as I am aware, is keen to defend the status quo, as represented by DSM. As Insel remarked in his blogpost: "Patients with mental disorders deserve better". The issue is whether RDoC is going to make things any better. I see five big problems.
1. McLaren (2011) is among those querying the assumption that mental illnesses are 'disorders of brain circuits'. The goal of the RDoC program is to fill in a huge matrix with new research findings. The rows of the matrix are not the traditional diagnostic categories: instead they are five research domains: Negative Valence Systems, Positive Valence Systems, Cognitive Systems, Systems for Social Processes, Arousal/Regulatory Systems, each of which has subdivisions: e.g. Cognitive Systems is broken down into Attention, Perception, Working memory, Declarative memory, Language behavior and Cognitive (effortful) control. The columns of the matrix are Genes, Molecules, Cells, Circuits, Physiology, Behavior, Self-Reports, and Paradigms. Strikingly absent is anything about experience or environment.
This seems symptomatic of our age. I remember sitting through a conference presentation about a study investigating whether brain measures could predict response to cognitive behaviour therapy in depression. OK, it's possible that they might, but what surprised me was that no measures of past life events or current social circumstances were included in the study. My intuitions may be wrong, but it would seem that these factors are likely to play a role. My impression is that some of the more successful interventions developed in recent years are based not on neurobiology or genetics, but on a detailed analysis of the phenomenology of mental illness, as illustrated, for example, by the work of my colleagues David Clark and Anke Ehlers. Consideration of such factors is strikingly absent from RDoC.
2. The goal of the RDoC is ultimately to help patients, but the link with intervention is unclear. Suppose I become increasingly obsessed with checking electrical switches, such that I am unable to function in my job. Thanks to the RDoC program, I'm found to have a dysfunctional neural circuit. Presumably the benefit of this is that I could be given a new pharmacological intervention targeting that circuit, which will make me less obsessive. But how long will I stay on the drug? It's not given me any way to cope with the tendency of checking the unwanted thoughts that obtrude into my consciousness, and they are likely to recur when I come off it. I'm not opposed to pharmacological interventions in principle, but they tend not to have a 'stop rule'.
There are psychological interventions that tackle the symptoms and the cognitive processes that underlie them more directly. Could better knowledge of neurobiological correlates help develop more of these? I guess it is possible, but my overall sense is that this translational potential is exaggerated – just as with the current hype around 'educational neuroscience'. The RDoC program embodies a mistaken belief that neuroscientific research is inherently better than psychological research because it deals with primary causes, when in fact it cannot capture key clinical phenomena. For instance, the distinction between a compulsive hand-washer and a compulsive checker is unlikely to have a clear brain correlate, yet we need to know about the specific symptoms of the individual to help them overcome them.
3. Those proposing RDoC appear to have a naive view of the potential of genetics to inform psychiatry. It's worth quoting in detail from their vision of the kinds of study that would be encouraged by NIMH, as stated here:
Recent studies have shown that a number of genes reported to confer risk for schizophrenia, such as DISC1 (“Disrupted in schizophrenia”) and neuregulin, actually appear to be similar in risk for unipolar and bipolar mood disorders. ... Thus, in one potential design, inclusion criteria might simply consist of all patients seen for evaluation at a psychotic disorders treatment unit. The independent variable might comprise two groups of patients: One group would be positive and the other negative for one or more risk gene configurations (SNP or CNV), with the groups matched on demographics such as age, sex, and education. Dependent variables could be responses to a set of cognitive paradigms, and clinical status on a variety of symptom measures. Analyses would be conducted to compare the pattern of differences in responses to the cognitive or emotional tasks in patients who are positive and negative for the risk configurations.
This sounds to me like a recipe for wasting a huge amount of research funding. The effect sizes of most behavioural/cognitive genetic associations are tiny and so one would need an enormous sample size to see differences related to genotype. Coupled with an open-ended search for differences between genotypes on a battery of cognitive measures, this would undoubtedly generate some 'significant' results which could go on to mislead the field for some time before a failure to replicate was achieved (cf. Munafò, & Gage, 2013).
The NIMH website notes that "the current diagnostic system is not informed by recent breakthroughs in genetics". There is good reason for that: to date, the genetic findings have been disappointing. Such associations as are found either indicate extremely rare and heterogeneous mutations of large effect and/or involve common genetic variants whose small effects are not of clinical significance. We cannot know what the future holds, but to date talk of 'breakthroughs' is misleading.
4. Some of the entries in the RDoC matrix also suggest a lack of appreciation of the difference between studying individual differences versus group effects. The RDoC program is focused on understanding individual differences. That requires particularly stringent criteria for measures, which need to be adequately reliable, valid and sensitive to pick up differences between people. I appreciate that the published RDoC matrices are seen as a starting-point and not as definitive, but I would recommend that more thought goes into establishing the psychometric credibility of measures before embarking on expensive studies looking for correlations between genes, brains and behaviour. If the rank ordering of a group of people on a measure is not the same from one occasion to another, or if there are substantial floor or ceiling effects, that measure is not going to be much use as an indicator of an underlying construct. Furthermore, if different versions of a task that are supposed to tap into a single construct give different patterns of results, then we need a rethink – see e.g. Foti et al, 2013; Shilling et al, 2013, for examples. Such considerations are often ignored by those attempting to move experimental work into a translational phase. If we are really to achieve 'precision medicine' we need precise measures.
5. The matrix as it stands does not give much confidence that the RDoC approach will give clearer gene-brain-behaviour links than traditional psychiatric categories.
For instance, BDNF appears in the Gene column of the matrix for the constructs of acute threat, auditory perception, declarative memory, goal selection, and response selection. COMT appears with threat, loss, frustrative nonreward, reward learning, goal selection, response selection and reception of facial communication. Of course, it's early days. The whole purpose of the enterprise is to flesh out the matrix with more detailed and accurate information. Nevertheless, the attempts at summarising what is known to date do not inspire confidence that this goal will be achieved.
After such a list of objections to RDoC, I do have one good thing to say about it, which is that it appears to be encouraging and embracing data-sharing and open science. This will be an important advance that may help us find out more quickly which avenues are worth exploring and which are cul-de-sacs. I suspect we will find out some useful things from the RDoC project: I just have reservations as to whether they will be of any benefit to psychiatry, or more importantly, to psychiatric patients.
References
Foti, D., Kotov, R., & Hajcak, G. (2013). Psychometric considerations in using error-related brain activity as a biomarker in psychotic disorders. Journal of Abnormal Psychology, 122(2), 520-531. doi: 10.1037/a0032618
Frances, A. (2013). Saving normal: An insider's revolt against out-of-control psychiatric diagnosis, DSM-5, big pharma, and the medicalization of ordinary life. New York: HarperCollins.
Kendell, R., & Jablensky, A. (2003). Distinguishing between the validity and utility of psychiatric diagnoses. American Journal of Psychiatry, 160, 4-12.
McLaren, N. (2011). Cells, Circuits, and Syndromes: A Critical Commentary on the NIMH Research Domain Criteria Project Ethical Human Psychology and Psychiatry, 13 (3), 229-236 DOI: 10.1891/1559-4343.13.3.229
Munafò, M. R., & Gage, S. H. (2013). Improving the reliability and reporting of genetic association studies. Drug and Alcohol Dependence(0). doi: http://dx.doi.org/10.1016/j.drugalcdep.2013.03.023
Shilling, V. M., Chetwynd, A., & Rabbitt, P. M. A. (2002). Individual inconsistency across measures of inhibition: an investigation of the construct validity of inhibition in older adults. Neuropsychologia, 40, 605-619.
This article (Figshare version) can be cited as:
Bishop, Dorothy V M (2014): Changing the landscape of psychiatric research: What will the RDoC initiative by NIMH achieve?. figshare. http://dx.doi.org/10.6084/m9.figshare.1030210
P.S.8th October 2015.
RDoC is in the news again, leading Jon Roiser to send me a tweet asking whether my views expressed re social factors were just intuitions or evidence-based. That's a good question, given the importance I attach to evidence. So is there any evidence that past life events or current social situation predict response to intervention in depression?
I have to confess I am not an expert in this area. My views are largely formed from what I learned years ago when training as a clinical psychologist, when research by Brown and Harris showed life events were potent predictors of depression:
Brown, G.W. & Harris, T.O. (1978). Social origins of depression: A study of psychiatric disorder in women. London: Tavistock.
These studies were not on intervention, but it does seem plausible that the same factors that are associated with initial onset will also influence response to intervention. Thus it seems reasonable that it would be harder to treat someone's depression if they are still experiencing the factors that led to the initial depression, e.g. living in an abusive relationship, coping with the death of a loved one, or experiencing financial stress.
In response to Jon's query, I did a small trawl through recent articles in Web of Science; I have only looked at abstracts for these, so don't know how good quality the evidence is, but the general impression is that social factors and life events are still regarded as important factors in the etiology of depression - and therefore might also be expected to influence response to intervention. Here's a handful of papers:
Colman, I., Zeng, Y., McMartin, S. E., Naicker,
K., Ataullahjan, A., Weeks, M., . . . Galambos, N. L. (2014). Protective
factors against depression during the transition from adolescence to adulthood:
Findings from a national Canadian cohort. Preventive Medicine, 65,
28-32. doi: 10.1016/j.ypmed.2014.04.008
Cwik, M., Barlow, A., Tingey, L., Goklish, N.,
Larzelere-Hinton, F., Craig, M., & Walkup, J. T. (2015). Exploring Risk and
Protective Factors with a Community Sample of American Indian Adolescents Who
Attempted Suicide. Archives of Suicide Research, 19(2), 172-189. doi:
10.1080/13811118.2015.1004472
Dour, H. J., Wiley, J. F., Roy-Byrne, P.,
Stein, M. B., Sullivan, G., Sherbourne, C. D., . . . Craske, M. G. (2014). Perceived
social support mediates anxiety and depressive symptom changes following
primary care intervention. Depression and Anxiety, 31(5), 436-442. doi:
10.1002/da.22216
Kemner, S. M., Mesman, E., Nolen, W. A.,
Eijckemans, M. J. C., & Hillegers, M. H. J. (2015). The role of life events
and psychological factors in the onset of first and recurrent mood episodes in
bipolar offspring: results from the Dutch Bipolar Offspring Study. Psychological
Medicine, 45(12), 2571-2581. doi: 10.1017/s0033291715000495
Sheidow, A. J., Henry, D. B., Tolan, P. H.,
& Strachan, M. K. (2014). The Role of Stress Exposure and Family
Functioning in Internalizing Outcomes of Urban Families. Journal of Child
and Family Studies, 23(8), 1351-1365. doi: 10.1007/s10826-013-9793-3
I'd be happy to consider alternative evidence, but my view is that if we want to look at brain or gene predictors, we'd do well to also assess life events and social factors - things that are relatively easy to measure, might explain a significant proportion of variance, and could also possibly provide a mechanism to account for neurobiological findings.
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You make some important points, and you’re right, these are “early days” — but too early, perhaps, to arrive at such a pessimistic conclusion about RDoC’s clinical potential? I’ll quote its stated purpose:
ReplyDelete“RDoC is intended as a framework to guide classification of patients for research studies, not as an immediately useful clinical tool. While the hope is that a new way forward for clinical diagnosis will emerge sooner rather than later, the initial steps must be to build a sufficient research foundation that can eventually inform the best approaches for clinical diagnosis and treatment.”
Of course, RDoC is only going to be as good as the science that goes in to it. I expect they’ll continue to develop and improve in parallel. The fact is that our current system of forcing heterogeneous patients into ever-changing discrete categories—collapsing over what could be meaningful variation—is antiquated and untenable. You acknowledge that nobody is happy with the status quo. What, then, is the alternative, if not a graded, data-driven approach like RDoC?
With regard to your point # 1, life circumstances and experience should absolutely be considered in treatment decisions, and should be operationalized for RDoC. It’s hard to see how PTSD, for example, could ever be treated without taking this into account.
I hope you'll consider pointing the RDoC folks to this post. Their website says they want its development to be open and welcome comments and discussion.
thanks Kyle. I agree something may come of this, but I am deeply uneasy about NIMH putting all of its eggs into this one basket. I hear, for instance, from colleagues in the US that NIMH is no longer willing to fund comparative psychotherapy outcome studies in which a new psychological treatment is compared with a gold standard psychological therapy to see if it is an advance. That seems incredibly short-sighted to me.
DeleteNice and informative information shared by your blog. I really appreciate it.
DeleteAmerican Psychiatric Association
As I wrote in an article on DxSummit.org ("Lead, Follow, or Get out of the Way -- A Layman Perspective on Change -- September 2013), "...while continued research seems warranted in brain neurology for emotion, perception, learning and other functions, it seems deeply implausible to expect brain research to produce highly targeted and effective medications for problems deemed mental in their presentation. Brain processes can accurately be characterized as redundant, multi-factorial, thresholded, non-linear, self-adaptive, distributed and stochastic—terms recognizable to many engineers, but to relatively few medical practitioners or medical researchers. The net impact of these dimensions is that many of the brain’s internal processes inherently cannot be observed, isolated or safely modified under rigorous experimental conditions. Thus expecting neurology to replace psychology seems simplistic and naive."
ReplyDeleteAlthough the idea quite probably horrifies many in the psychiatric profession, I believe professionals need to seriously examine criticism now being levied against them from lay people and their braver colleagues. Not only do psychiatrists not know how to characterize mental disorder and distress, but it is possible that the entire medical disease model is itself inappropriate and destructive. From this point of view, enabling the patient to function in their world has taken a back seat to exerting social controls of social conformity. It is indeed conceivable that in many large issues, Thomas Szasz may have been right: madness may turn out to be largely a manufactured entity of social control.
Thanks for your comment. Although we agree on some points, I can't accept your final comment. I think part of the problem we have is that people have been polarised between a neurobiological stance at one end and a 'social construct' view of mental disorder at the other. Both are too simplistic, I think. Yes, social factors will influence rates of mental disorder and how it presents, but to deny any role of genetics and biology is to ignore a wealth of evidence to the contrary.
Deleteit seems that the transitory, multi dimensional, chaotic phenomena... "mind" will make sense if we quit asking the old way and just look, agnostically, at brain. I'm not privy to the methodology this RDoC project proposes, what statistic crucnhers it has in its shop, but i certainly hope some bell labs, cdma geeks are consulted, since its true that 'randomwalk' and 'stochastics' are not commonly dropping from the lips of clinicians. Indeed, I only became aware of the powerful Beyseian approach from cdma communications engineers.
ReplyDeleteinteresting developement and if you have any leads on a Nitrogen Vacancy in Diamond fMRI Reciever, call me asap
stay orthogonal
As Kyle said, you made some very important points. I haven't seen too many critiques from Americans in a position to receive funding from NIMH!
ReplyDeleteIn a post from last year (What RDoC Research Might Look Like), I noted some similar problems with embracing diagnostic messiness:
"One potential pitfall of this approach is the money required to enroll huge numbers of patients. If commonalities in cognitive function or brain circuitry or especially genetic risk factors are to emerge from studying all patients with mood disorder-like symptoms, then sample sizes must be very large to overcome potential noise in the system(s)."
It's not clear to me that anhedonia in major depression, for instance, is the same as anhedonia in schizophrenia, and whether it'll ultimately be a good idea to treat the two in the same way. Likewise, does a common alteration in reward circuitry lead to different DSM-esque categories like drug and alcohol use disorders, serious gambling problems, and mania? In an extreme view of the individual differences approach, we might even assume that each person has a unique version of some disorder, especially when taking into account environment and life experiences.
In theory, I do see RDoC as a way forward in linking brain to behavior, but it's unclear how well (and when) this new framework will translate into improved treatments.
Thanks for the link - I am coming at this from a different direction - my interest is in classification of neurodevelopmental disorders, and it is good to be pointed to some of the psychiatric issues and commentaries.
DeleteThe sample size issue might not be insuperable with large multicentre studies, but it's worrying that there seems little awareness of just how big samples would need to be in the genetics domain.
I could not be more skeptical about the "educational neuroscience" hype. But perhaps one of the reasons the results have been disappointing is because few studies have received the sort of funding (as Neuroskeptic points out) that would enable them to generate the kind of results that could be used as the foundation of meaningful real life intervention.
ReplyDeleteNow, I suspect, that in the majority of cases there is nothing there to be found - or rather, effects are there but they are so tiny as to be meaningless for any practical application In general, solving problems in the classrooms with neuroscience is about as useful as building bridges with quantum mechanics.
But even if we did come across some straightforward interventions (maybe even the ever elusive genetic diagnostic fingerprint or a cheap and reliable brainscan) the biggest danger I see is the drunk-under-the-lamp-post fallacy that's plaguing so much research in this area. We'll end up only studying things that we can measure with he tools of genetics and neuroscience and thus metaphorically looking for our keys where the light is, not where we lost them.
The science cargo cult is already rampant in education and psychology and it's moving us forward at glacial speed. Maybe we need funding for studies that use the right tools for the job. Large sample sizes for brain functional studies, and more advanced, replicable qualitative methods for education research.
BTW: I did notice a slight inconsistency of policy in your copyright notice. You only give license for reproduction of 50 word samples without permission. Yet, you reproduce 150 words from somebody else's text (without acknowledging permission). I can imagine what sort of things might have precipitated this. But wouldn't a Creative Commons BY NC-SA license accomplish the same thing but keeping with the spirit of the blogging community? Also, it might actually be legally enforceable whereas your homemade copyright notice probably is not.
Just responding to your BTW comment. I did remove that copyright notice - you are right in suggesting it is probably not capturing what I intend. Main aim is to avoid total ripoff by someone just reposting my posts, unattributed, on a monetised site - this has happened in the past, and is irritating.
DeleteAt suggestion of Jon Brock, I am now taking a different approach and for my more academic posts, am putting them up on Figshare, where they have a DOI. I don't think that will protect me from hijacking of my material, but it will make it easier to trace to source for those who have legitimate reasons for wanting to cite. We'll see how it goes.
Thank you Dorothy, as ever you have nailed an apparently attractive notion. I worry as well that the idea is growing among psychiatrists that only by being neuropsychiatrists can they survive and gain acceptance by the rest of medicine. The problem, as you point out, is that the neurocircuitry story is only one level of decription of brain process, and there is no reason in principle to prefer it to the behavioural level favoured by DSM, or the psychodynamic/ systemic analysis favoured by some psychologists and therapists. The test of what level to use in a given situation is simple: what will help the predicament of the person in front of you. I fear the NIMH have forgotten this.
ReplyDeleteMax
I agree with you Max and Dorothy, I love this article. As a student of developmental cognitive neuroscience. There is an allure to being on the side of neuroimaging, it looks more 'objective', but it is just a pretty picture of the brain. Neuroimaging is a proxy of a proxy, yet clear and insightful comments have been made from this methodology. Nevertheless, should we disregard behavioural and cognitive correlates, I think not. We are not bound by genes and neurobiology, they may exist and obviously like all life, are indirect causes of existence, but they do not explain the underlying putative mechanisms of a developmental psychopathology. We must look at the difference between social, past and rearing history since we are ignoring scientific discoveries that had really made people enquire about what makes us human. Also, from the paper by Hayiou-Thomas and colleagues in 2005, they had found the heritability of SLI and NLI was as a result of ascertainment biases, and that they found the heritability values was far less than originally expected. This suggests that we need to look at how we need to recruit participants.
ReplyDeleteFinally, a seminal paper by Henrich et al. (2010) posted WEIRD people, which I believe is an absolute must for a field on developmental psychology. Through the perusal of this article, I have noticed that autism a disorder we claim to know much about is discrepant in other cultures. Autism does not have difficulties in social impairments, communicative interactions and repetitive and social stereotyped behaviours. I know this is an over-simplification, yet in Eastern cultures, it is known that social impairments in males is seen sometimes typical as it is expected for them to be act distant and aloof. So does that mean we can say individuals from Eastern cultures are autistic? Obviously not, and I do know this is an oversimplification of a culture, but one to bear in mind.
So in summary we should be using the Uta Frith's model to merge genetics, cognition and behaviour with the environment. They all modify one another against a different standard and from an evolutionary viewpoint, we require the environment to modify our genetics, cognition and behaviour. As Max says, I fear not only NIMH has forgotten this, but so has research. These criticisms are placed under an inept or trivial within psychology, yet these factors define who we are and how to behave. So is NIMH at fault, I think so, but should we blame them entirely. I think we have to give a benefit of the doubt since they are just trying to synthesise and evaluate the information they can. The criteria they are providing is not stringent that we have to find every symptom, but as a guide to help us. We need clinicians who know these areas to provide evaluative information and to help us analyse and evaluate definitions.
I hope this makes sense.
Just read this excellent piece by Allen Frances that's v. relevant to this topic:
ReplyDeletehttp://www.psychologytoday.com/blog/saving-normal/201407/will-650-million-solve-the-mystery-mental-illness
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