Smart People Say They're Less Depressed

The questionable validity of self-report measures in psychiatry has been the topic of a few recent  posts here at Neuroskeptic.

Now an interesting new study looks at the question in issue from a new angle, asking: what kind of people report feeling more or less depressed? Korean researchers Kim and colleagues found that intelligence and personality variables were both linked to the tendency to self-rate depression more severely.

The study involved 100 patients who'd previously suffered from an episode of depression or mania and who, according to their psychiatrist, had now recovered and were back to normal. Kim et al looked to see what the patient thought about their mood, by getting them to complete the Beck Depression Inventory (BDI) self-report questionnaire.

This was compared to the clinican-administered HAMD scale (another Neuroskeptic favourite) which is meant to be independent of self report.

It turns out that the BDI and HAMD scores were only weakly correlated - with a coefficient of just r=0.32. That's really not very good considering that, in theory, they both measure the same thing: 'depression'. Many people reported being considerably depressed when their clinicians rated them as fine.

But more interestingly, certain characteristics of the patients were correlated with their self-report/clinician-rating discrepancy. Specifically, patients with a lower IQ, who were more impulsive, and less conscientious, tended to self-report more severe depression.

Now, the uncharitable interpretation of these people is that they were just too sloppy to complete the form properly... the uncharitable interpretation of the psychiatrists is that it's their fault for underestimating depression in people less inclined to express themselves in 'the right way'. There's no way to know.

Either way, it's a serious problem because it shows that self-report and observer-report measures of depression aren't just poorly correlated, they're actually measuring different things for different people.

It could be even worse than it appears because the HAMD, although supposedly not a self-report measure, does in fact heavily rely on the patient's cooperation. So a 100% clinician-rated scale might be even further removed from self-report.

Kim EY, Hwang SS, Lee NY, Kim SH, Lee HJ, Kim YS, and Ahn YM (2012). Intelligence, temperament, and personality are related to over- or under-reporting of affective symptoms by patients with euthymic mood disorder. Journal of affective disorders PMID: 23270973

When "Mental" Illness Isn't

 

There's a theory that 'psychiatric diseases' like depression and schizophrenia aren't diseases because they're not diagnosed on the basis of any kind of biological abnormality, but purely on symptoms - unlike 'real' diseases like cancer and AIDS.

Now, in my view there's quite a bit of truth in that - but there's also a serious flaw in the argument. Sometimes, disorders diagnosed on the basis of psychiatric symptoms do turn out to have had a clear biological cause. So the original diagnosis of a psychiatric disease was correct: there was indeed a disease.

This is happening more and more often now because of biomedical advances.

A group of German neurologists and psychiatrists recently wrote about a case of a man diagnosed with bipolar disorder:

In February 2009, a 28-year-old presented to our clinic with a first episode of depression. He reported depressed mood, anhedonia, decreased drive, reduced alertness and concentration. The symptoms responded well to quetiapine 100 mg.

Fourteen months later, a first manic episode with logorrhea [excessive speech], aggressive and disinhibited behavior occurred... it completely remitted after treatment with quetiapine 1000mg. A diagnosis of bipolar I disorder was made.

Two months later, the patient presented with another depressive episode... Despite treatment with quetiapine, aripiprazole, lithium, valproate and escitalopram, the patient did not improve...

So far, seems like a fairly typical case of bipolar. However, it turned out that...

Neurological examination was remarkable for extrapyramidal symptoms with left-sided rigor and bradykinesia [slowed movements]. On initial and concurrent magnetic resonance imaging (MRI), numerous subcortical lesions in the frontal lobes were detected... Screening for autoimmune antibodies detected NMDAR antibodies.

It turned out the guy had autoimmune encephalitis: his body was generating antibodies that blocked the brain's key NMDA receptors; the drug ketamine does that too. Treatment with immunosuppressant drugs was started and he recovered fairly quickly. For a first-hand account of the disease, in which it was also diagnosed as a psychiatric disorder initially, see the recent book Brain On Fire.

Now, let's imagine that this had happened in 1960. What would the guy's story have been then?

He'd have been seen by a psychiatrist and diagnosed with bipolar, just as he was today. Depending on how severe the depression was, and whether or not he had any more episodes, he might well have ended up in a psychiatric hospital.

But he probably wouldn't have been diagnosed with a neurological disorder. He'd have tested negative for all the neurological diseases known at the time. No-one tested for NMDA antibodies back then, because NMDA receptors weren't even discovered until 1981.

It's true that his neurological exam showed a movement disorder (left-sided rigor and bradykinesia)  but this might well have been written off as a side effect of the high dose antipsychotics he was taking, which cause similar movement disorders.

50 years ago this guy, and many others like him, could well have ended up committed to an asylum. 100 years ago, I think it would have been almost certain he'd have been deemed 'insane' and locked up at some point.

If so, some of the people in psychiatric hospitals 50 or 100 years ago will have had this disease - or others. And if we didn't know about anti-NMDA encephalitis until recently, who's to say what we'll discover next?

Choe CU, Karamatskos E, Schattling B, Leypoldt F, Liuzzi G, Gerloff C, Friese MA, and Mulert C (2012). A clinical and neurobiological case of IgM NMDA receptor antibody associated encephalitis mimicking bipolar disorder. Psychiatry research PMID: 23246244

Ketamine: Magic Antidepressant Or Illusion? Revisited

There's a lot of interest in the idea that ketamine provides unparalleled rapid, powerful antidepressant effects, even in people who haven't responded to conventional antidepressants.

Earlier this year, I asked:

Ketamine - Magic Antidepressant, or Expensive Illusion?
There have now been several studies finding dramatic antidepressant effects of ketamine, the "club drug" aka "horse-tranquilizer". Great news? If you believe it. But hold your, er, horses... there's a problem.

My concern was that although depressed patients certainly do report feeling better after an injection of ketamine, compared to people given placebo, that doesn't prove that the drug is actually an antidepressant.

Rather, patients might be experiencing an enhanced, 'active' placebo effect, because ketamine causes subjectively powerful hallucinogenic experiences. So the placebo-controlled trials weren't really blinded.

To settle the question, I suggested a three-way trial comparing it both to an inert placebo, and to some other hallucinogen; if ketamine has a specific antidepressant effect, it should produce more improvement than the comparison drug.

This has never been done.

Given this background, a new trial from NIMH's Ketamine King, Carlos Zarate, makes interesting reading: A Randomized Trial of a Low-Trapping Nonselective N-Methyl-D-Aspartate Channel Blocker in Major Depression.

Zarate et al tried a novel drug, AZD6765 in depressed people. AZD6765 works much like ketamine in that it blocks brain NMDA receptors. But it is a less powerful trapping blocker than ketamine, meaning that AZD6765 causes less dramatic effects on the target receptors, in some respects.

In practice, this makes AZD6765, much less hallucinogenic than ketamine.

So it's interesting that, compared to placebo, the new drug only produced small benefits. On the MADRS depression symptom scale, patients felt a little better on AZD6765, but the boost only lasted a few hours.

The effect was far smaller than in an earlier ketamine trial as my crudely-mashed-up graph shows (although note that the patient populations were somewhat different, one bipolar and one unipolar depression, although their baseline severity was the same.)

While on ketamine people experienced significant subjective effects, with AZD6765 they didn't, and couldn't tell whether they got drug or placebo. Is that why they got a smaller benefit?

This is what we'd see if NMDA blockers do have a modest antidepressant effect but the dramatic improvements seen on ketamine are largely active placebo phenomena. Then again, it's also consistent with ketamine being a powerful antidepressant and AZD6765 just being less effective because it's a milder blocker of NMDA - effectively, a low dose of ketamine.

To tell the difference, we need... an active placebo controlled trial, like I've been banging on about for ages. But I wasn't the first one to suggest it - that was none other than Carlos Zarate et al in 2006.


Zarate CA Jr, Mathews D, Ibrahim L, Chaves JF, Marquardt C, Ukoh I, Jolkovsky L, Brutsche NE, Smith MA, and Luckenbaugh DA (2012). A Randomized Trial of a Low-Trapping Nonselective N-Methyl-D-Aspartate Channel Blocker in Major Depression. Biological psychiatry PMID: 23206319

Ritalin, The Ultimate Crimefighter?

There's been lots of interest in the idea that ADHD meds reduce crime rates.

No doubt that, even as we speak, worried pundits are writing of how this is a worrying Orwellian scenario and yadda yadda. But what's really going on?

The research is from Sweden and published in the New England Journal of Medicine: Medication for Attention Deficit–Hyperactivity Disorder and Criminality. The first thing to note is that the study is not about giving medication in order to prevent crime; it was purely looking at what happened to people given ADHD treatment for their ADHD.

In a nutshell, the authors found that people diagnosed with ADHD were about 10% less likely to be convicted of a crime during periods when they were on medication for the disorder. This was true of both men and women, and the effect was greater for the more serious offences.

It was a huge study with over 25,000 ADHD patients and the data comprise pretty much everyone in Sweden over the relevant period so in that respect it's a very good study - although speaking of Orwellian, these studies are only possible because of the Scandinavian tendency to make national registers of everything.

Now the big criticism here is that it's just a correlation, it doesn't prove that the meds were what prevented crime. It might be that ADHD meds have no effect on crime, but that people are less likely to commit crimes at periods when they have their lives sorted out (when they're 'on the rails'), one marker of which is that they're seeking treatment for their ADHD.

However, the authors found that periods of use of SSRI antidepressants were not associated with changes in conviction rates. This is quite good evidence against the 'on the rails' critique, assuming that being prescribed SSRIs is as much a marker of being on the rails as being prescribed Ritalin is.

So, in my view, this is pretty good work, as good as any observational non-randomized study. However, remember: this is just about treating ADHD. Not drugging criminals to stop crime.

Lichtenstein P, Halldner L, Zetterqvist J, Sjölander A, Serlachius E, Fazel S, Långström N, and Larsson H (2012). Medication for attention deficit-hyperactivity disorder and criminality. The New England journal of medicine, 367 (21), 2006-14 PMID: 23171097

Exercise And Depression Revisited

A new study has found little evidence that aerobic exercise helps treat depression, contrary to popular belief.

Danish researchers Krogh and colleagues randomly 115 assigned depressed people to one of two exercise programs. One was a strenuous aerobic workout - cycling for 30 minutes, 3 times per week, for 3 months. The other was various stretching exercises.

The idea was that stretching was a kind of placebo control group on the grounds that, while it is an intervention, it's not the kind of exercise that gets you fit. It doesn't burn many calories, it doesn't improve your cardiovascular system, etc. Aerobic exercise is the kind that's most commonly been proposed as having an antidepressant effect.

So what happened? Not much. Both groups got less depressed but there was zero difference between the two conditions. The cyclists did get physically fitter than the stretchers, losing more weight and improving on other measures. But they didn't feel any better.

If this is true, it might mean that the antidepressant effects of aerobic exercise are psychological rather than physical - it's about the idea of 'exercising', not the process of becoming fitter.

While many trials have found modest beneficial effects of exercise vs a "control condition", the control condition was often just doing nothing much - such as being put on a waiting-list. So the placebo effect or the motivational benefits of 'doing something', rather than the effects of exercise per se, could be behind it. In the current study though the stretching avoided that problem.

As I said in a post about a previous paper, I said that Exercise and Depression: It's Complicated

The idea that exercise is a useful treatment for depression: it's got something for everyone. For doctors, it's attractive because it means they can recommend exercise - which is free, quick, and easy, at least for them - instead of spending the time and money on drugs or therapy. Governments like it for the same reason, and because it's another way of improving the nation's fitness. For people who don't like psychiatry, exercise offers a lovely alternative to psych drugs - why take those nasty antidepressants if exercise will do just as well? But this doesn't mean it's true.

This was a moderate sized study, and one study by itself doesn't prove much - any more than one single political poll does. From personal experience I think there's a good chance strenuous aerobic exercise can boost mood... but this is a reminder that the picture on exercise and depression is not quite as clear as the recent enthusiasm for it suggests...

Krogh J, Videbech P, Thomsen C, Gluud C, & Nordentoft M (2012). DEMO-II Trial. Aerobic Exercise versus Stretching Exercise in Patients with Major Depression-A Randomised Clinical Trial. PloS one, 7 (10) PMID: 23118981

Gene-Guided Antidepressants?

Over the past couple of years, "Big Pharma" has largely moved away from psychiatric drug development. This shift has been widely discussed.

But another trend has been happening over the same time period - or so it seems to me. This is the rise of small companies who offer techniques for diagnosing mental illness, or predicting which drugs will work best. Generally (it seems) partnerships between venture capitalists and psychiatry (ex-)researchers, these enterprises might be dubbed "Little Pharma".

The latest is a company called AssureRx Health, Inc. According to a paper just published, they offer

a pharmacogenomic algorithm designed to improve the safety and efficacy of prescribing antidepressant and antipsychotic medication... based on the genotyping of both copies of five genes.

From this, you end up with a report giving each drug a rating of green, yellow, or red (see above).

The price is not provided on their website.

According to the paper, they gave 26 depressed patients normal treatment at the discretion of their psychiatrist, while 25 got treatment guided by the AssureRx algorithm. It was non-randomized, and unblinded so there's a clear possibility of a placebo effect.

Anyway, the results were...

For the first 4 weeks of treatment, there was no difference between the two groups whatsoever in terms of depression symptom scores - they both improved. But then by week 8, the unguided patients abruptly got worse, while the AssureRx-guided ones continued to benefit. This is an unusual pattern of improvement in an antidepressant trial.

Previously, I wrote about another Little Pharma antidepressant prediction scheme. It used a  different approach, measuring brain electrical activity using a technique called "rEEG", rather than genetics. But the basic idea is the same... and so are the problems.

As I said last time:

There were two groups and they got entirely different sets of drugs. One group also got rEEG-based treatment personalization. That group did better, but that might have nothing to do with the rEEG: they might have done equally well if they'd just been assigned to [those drugs] by flipping a coin. We cannot tell, from these data, whether rEEG offered any benefits at all.

In the AssureRx paper, we can't even tell whether the two groups got different kinds of drugs, because the meds used aren't reported, but if they did differ then that would offer an alternative explanation for the differences in outcome: maybe the 'guidance' just recommended better drugs overall, with the genes being just a sideshow. Or maybe it's a placebo, as I said.

Moving on, I also wrote... 

What's curious is that it would have been very simple to avoid this issue. Just give everyone rEEG, but shuffle the assignments in the control group, so that everyone was guided by someone else's EEG. So you'd give control Patient 2 the drugs that Patient 1 should have got, and vice versa; swap 3 and 4, 5 and 6, etc.

This would be a genuinely controlled test of the personalization, because both groups would get the same kinds of drugs... and it would allow the trial to be double-blind: in this study the investigators knew which group people were in, because it was obvious from the drug choice...

It is odd that Little Pharma never seem to do such real vs. muddled prediction studies, as they'd be really informative as to whether their approach is a helpful innovation as opposed to an expensive, meaningless red herring. Hmm.

Hall-Flavin, D., Winner, J., Allen, J., Jordan, J., Nesheim, R., Snyder, K., Drews, M., Eisterhold, L., Biernacka, J., and Mrazek, D. (2012). Using a pharmacogenomic algorithm to guide the treatment of depression Translational Psychiatry, 2 (10) DOI: 10.1038/tp.2012.99

DSM-5 R.I.P?

Yesterday, the proposed new DSM-5 revision of the American Psychiatric Associations "Bible of Psychiatry" came under yet more criticism.

Aaron T. Beck, the father of currently-mega-popular cognitive behavioural therapy, started it off with an attack on the upcoming changes to one diagnosis, Generalized Anxiety Disorder; but many of the points also apply to the other DSM-5 proposals:

The lack of specific features, which is the primary issue for GAD, will not be addressed in DSM-5. The hallmark of the condition will remain pathological worry, although it also characterizes other disorders. Likewise, the proposed behavioral diagnostic criteria lack specificity for GAD, and it is not clear how these will be assessed. The proposed changes will lower the diagnostic threshold for GAD in DSM-5... many currently subthreshold cases will qualify for this diagnosis. The likely inclusion of many such "false-positives" will result in an artificial increase in the prevalence of GAD and will have further negative consequences.

Then from across the Atlantic, and also across the psychotherapy-vs-medication divide, came another piece of criticism. The authors are all associated with the European Medicines Agency (EMA, Europe's equivalent of the FDA), or with national drug regulators. Although they're writing in a personal capacity, this is still big news if you ask me.

These authors start out by saying that the EMA is broadly in favour of DSM reform, but they then attack one of the key DSM-5 innovations - the move towards 'dimensional measures' of symptoms in addition to diagnoses:

One of our main concerns is related to potential future [drug] indications based on an effect on a dimension that is independent of diagnostic categories (although we acknowledge that non-specific claims are common in other areas, such as analgesics for pain). As an example, cognitive impairments are common in psychiatric disorders, but they do not have a unique clinical pattern or a unitary cause.

We therefore believe that, at present, such a cross-cutting approach may increase heterogeneity in patient populations and make the assessment of the benefit–risk balance more difficult. Similarly, the use of dimensions as key secondary end points in many different diagnostic categories may lead to pseudospecific indications and polypharmacy. As a general rule, a therapeutic indication should be a well-recognized clinical entity that is clearly distinguishable from other conditions...

They also echo Beck in warning of over-diagnosis and over-medicalization:

Current proposals to reclassify some conditions that were subthreshold or prodromal as distinct syndromes or disorders could have implications for clinical trials. The inclusion of milder or very early cases of psychiatric disorders may lead to an increase in the number of non-disordered (false-positive) patients in clinical trials, and to an increase in the placebo effect, as less severe cases are more likely to respond to placebo. It may therefore be difficult to show a statistically significant difference [of drug over placebo]...

This raises another highly controversial issue: the risk of medicalization of the normal population. In this respect, a strong concern comes from the proposal to remove bereavement exclusion from the criteria for major depressive disorder, implying that all individuals with ‘normal grief’ might be considered as patients in the future.

Regular readers will remember that I've covered both overdiagnosis screwing up clinical trials, and the bereavement debate.

Two and a half years ago, shortly after the first draft of the DSM-5 was made public, I predicted that the eventual release of DSM-5 would be a non-event because, by then, it would have been widely debated and criticized, destroying the illusion of expert consensus that any such document must have in order to succeed.

I think events have borne this out. An awful lot of professionals, patients, and their relatives, will reject the changes in favour of sticking with the DSM-IV or other criteria. Without swift and general acceptance, a document like the DSM is just paper. It seems increasingly likely that the DSM-5 is going to be dead on arrival.

Starcevic V, Portman ME, & Beck AT (2012). Generalized anxiety disorder: between neglect and an epidemic. The Journal of nervous and mental disease, 200 (8), 664-7 PMID: 22850300

Florence Butlen-Ducuing et al (2012). DSM‑5 and clinical trials in psychiatry: challenges to come? Nature Reviews: Drug Discovery DOI: 10.1038/nrd3811

Big Pharma Read Neuroskeptic?

A few weeks back I blogged about an error-ridden paper from pharmaceutical company Janssen. It  reported on the failure of a candidate antidepressant, JNJ-18038683. But it was rubbish: the Abstract contradicted the results of the study, wrongly claiming that the drug did statistically significantly better than placebo in a particular analysis, when it didn't. And they repeatedly mixed up the names of two other antidepressants.

I posted on May 17th. On May 23rd, a new version of the offending article quietly appeared on the journal's website: here it is. But the old version is still up, although I'm not sure it's intended to be, because the link is gone, so I think the only way to find it is from this blog.

Interestingly, the new manuscript corrects those two issues I noted. As far as I can see those are the only changes. Coincidence?

The original paper was a "Fast Forward" online accelerated publication manuscript, and it's common for these to be corrected in minor ways when they're officially published (i.e. when they appear in print), but that's not what happened here, because the new version is still a Fast Forward. This kind of revision is unusual.

So it seems that someone at Janssen is reading this blog!

If so: Hey. Believe it or not, I'm on your side, I want you to succeed. I suffer from depression, and I've love it if you came up with an actually good new antidepressant. But your industry hasn't released one in at least 10 years (be honest), and you're not fooling anyone with clever statistical tricks.

Forget that, and invest in some proper science. For example, ketamine is clearly the most exciting potential antidepressant right now, and glutamate could be the next serotonin. But because no-one has tested it against an active placebo, no-one, including you, knows whether it's really working. Run a really serious trial of ketamine, if it does work, then that's your next generation of antidepressants right there. If not, better to know that now than later when you've sunk billions into the idea.

That Antidepressants In Water Cause Autism Study

Oh dear. The newspapers this morning are reporting that

Autism 'could be triggered by very low doses of anti-depressants or other chemicals found in water supply'

Here's the study. Young fish were exposed to a combination of three drugs, two antidepressants and an epilepsy med, for 18 days.

First off, this study was tiny with an effective sample size of just 6. Three tanks of fish got exposed to the drugs, and three control tanks didn't. There were multiple fish per tank, five in fact, but those are not five independent observations, because they shared a tank. That's just tiny for a drug trial, or any scientific study really.

Next, the drug doses were much higher than in the water supply. Levels of fluoxetine (Prozac) were 700 times higher than observed in drinking water, for carbamazapine it was 400 times higher. And that's based on the authors' figures for drinking water which they admit are "the highest observed concentrations from various systems". The authors defend this by saying that in drinking water there will be other related compounds, on top of the drugs themselves, adding up to a higher dose. OK - but 400, 700 times higher? We've no idea if that's realistic. They don't justify this number.

What did the drugs actually do to the fish? After 18 days of exposure to the drugs, the fish - juvenile fathead minnows - had their brains removed and the expression levels of various genes measured using a genetic microarray.

The drugged minnows had significantly increased expression of a set of 324 genes dubbed "autism genes" ("autism_ideopathic" in the paper.) I'm not going to get into the question of whether these really are autism genes in humans, or whether fish brains are a good of model of humans. Those are hard issues. But what's easy to see is that while this set of genes were apparantly increased, so were many others. It was not specific to 'autism genes'.

The autism genes were upregulated by an average factor of +1.621... but this was only slightly more than the "Parkinson's Disease genes" at +1.56 and the "Multiple Sclerosis" ones at +1.375. Meanwhile, "Bipolar Disorder" genes were down by -1.172. So if antidepressants in the water are causing autism, they're probably also causing (or preventing!) a lot of other problems too.

The authors note that only three of the gene sets were statistically significantly altered, but that doesn't mean those sets were special, this is the fallacy of treating differences in significance levels as evidence of significant differences.

Of 10 more specific "autism gene" sets that they also examined (in the same fish), all were increased by various amounts (+1.050 to +1.537), some of which were significant - but one of those was a set of genes previously reported decreased in autistics, not increased (it was the "synapse" genes from this study).

What these changes in gene expression mean is anyone's guess. Given the small sample size they could be just noise. If not, all they really show is that levels of psychoactive medications that are quite low, but much higher than in drinking water, have affect the brains of fish. We don't know what that effect means, for the fish, let alone humans.

Early life antidepressant exposure might cause autism. I don't know. Stranger things have happened. We know that fetal anticonvulsant exposure can do it but that's when mothers are actually taking the pills. It's one giant leap from that to traces in drinking water. It's the difference between falling off your chair and falling off the Empire State Building.

Michael A. Thomas, and Rebecca D. Klaper (2012). Psychoactive Pharmaceuticals Induce Fish Gene Expression Profiles Associated with Human Idiopathic Autism PLoS ONE

Bipolar Disorder - A BRIDGE to nowhere?

Last August I blogged about a research paper that claimed that almost half of all people suffering from depression actually have features of bipolar disorder - including me: So Apparantly I'm Bipolar

It was called the BRIDGE study. I took issue with it for various reasons, including the fact that it counted as 'bipolar features' any periods of irritable or elevated mood, even if they were associated with drug treatment:

Under the new regime if you've ever been irritable, high, agitated or hyperactive, on antidepressants or not, you meet "Bipolar Specifier" criteria, so long as it was marked enough that someone else noticed it...

A cynic would say that this is a breathtaking piece of psychiatric marketing. You give people antidepressants, then you diagnose them with bipolar on the basis of their reaction to those drugs, thus justifying selling them yet more drugs.

The cynic would not be surprised to learn that this study was sponsored by pharmaceutical company Sanofi. 

Now a crack team of psychiatrists have written a Letter to the Editor criticizing BRIDGE and they say... pretty much what I said: BRIDGE Study Warrants Critique. They do make a couple of new points also.

The 8 authors of the Letter include David Allen, David Healy, Peter Parry and Jon Jureidini, all major critical voices in psychiatry. However... while this A-Team make an excellent case that BRIDGE is a step in the direction of overdiagnosis and overtreatment of bipolar, they drop the ball slightly when they say:

The article concluded with an appeal to use “mood stabilizers,” presumably atypical antipsychotics, which are less efficacious than lithium. The sponsor has a medication in this class.

Sanofi does make the atypical antipsychotic amisulpiride, but it's not generally referred to as a "mood stabilizer", and I'm not sure why you'd assume that Sanofi had amisulpiride specifically in mind. The BRIDGE team exploit this in their rebuttal letter:

Allen et al cast unseemly aspersions that the BRIDGE study was a vehicle to promote sales of an antipsychotic drug sold by sanofi-aventis. sanofi-aventis has no antipsychotic with an indication for bipolar disorder. We know of no evidence that this was the case at any stage of development and execution of the BRIDGE study.

Maybe so, but as I said in my post, Sanofi also make some popular brands of valproate/valproic acid, a prototypical "mood stabilizer" which is widely used in bipolar disorder. I'd have said that was the more likely candidate...

Fundamentally, we know that Sanofi "was involved in the study design, conduct, monitoring, data analysis, and preparation of the report." We also know that Sanofi is exists to make profit by selling drugs. So either Sanofi thought that this study would make them a profit eventually, by selling more drugs... or they threw money and time at this for no commercial reason. Hmm.

The reply concludes with the frankly bizarre statement that:

Allen et al view their position as part of a “debate” about the “ever-widening bipolar spectrum.” We consider data, not debates, as central to the progress in the scientific understanding of mood disorders...

But science is a debate about data. Data by themselves are just numbers; to be useful, they must be interpreted, and scientific debates aim at arriving at such interpretations. No-one is questioning the BRIDGE data as such, we're questioning what it means.

David M. Allen, et al (2012). BRIDGE Study Warrants Critique Archives of General Psychiatry, 69 (6) DOI: 10.1001/archgenpsychiatry.2012.118

Another Antidepressant Crashes & Burns

Yet another "promising" novel antidepressant has failed to actually treat depression.

That's not an uncommon occurrence these days, but this time, the paper reporting the findings is almost as rubbish as the drug: Translational evaluation of JNJ-18038683, a 5-HT7 receptor antagonist, on REM sleep and in major depressive disorder

So, Pharma giant Janssen invented JNJ-18038683. It's a selective antagonist at serotonin 5HT-7 receptors, making it pharmacologically rather unusual. They hoped it would work as an antidepressant. It didn't - in a multicentre randomized controlled trial of 230 depressed people, it had absolutely no benefits over placebo. A popular existing drug, citalopram, failed as well:

About the only thing JNJ-18038683 did do in humans was to reduce the amount of dreaming REM sleep per night. This REM suppressing effect is also seen with other antidepressants and this is evidence that the drug does do something - just not what it's meant to. Being charitable you could call this a failed trial.

Ouch! But it gets better. Unhappy that JNJ-18038683 bombed, Janssen reached for their copy of the Cherrypicker's Manifesto. This is a new statistical method, proposed by fellow Pharma company GSK in a 2010 paper, which consists of excluding data from study centres with a very high (or very low) placebo response rate.

Anyway, after applying this "filter" JNJ-18038683 seemed to do a bit better than placebo, but the benefit over placebo still wasn't statistically significant - with a p value of 0.057, the wrong side of the sacred p=0.05 line (on page 33).
Yet Page 33's "trend towards statistical significance" magically becomes "significant" - in the Abstract:

[with] a post hoc analyses (sic) using an enrichment window strategy... there was a clinically meaningful and statistically significant difference between JNJ-18038683 and placebo.

Well, no, there wasn't actually. It was only a trend. Look it up.

That aside, the problem with the whole filter idea is that it could end up biasing your analysis in favour of the drug, leading to misleading results. The original authors warned that "data enrichment is often perceived as a way of improperly introducing a source of bias... In conventional RCTs, to overcome the bias risk, the enrichment strategy should be accounted for and pre-planned in the study protocol." They should know, as they invented it, but Janssen rather oddly say the exact opposite: "This methodology cannot be included in a protocol prospectively as it will introduce operational bias in that scheme."

Hmm.

Anyway, even after the filter technique, citalopram didn't work either... bad news for citalopram, except, was it citalopram at all? This is really unbelievable: Janssen don't seem clear on whether they compared their drug to citalopram, or to escitalopram - a quite different drug.

They say "citalopram" in most cases, but they have "escitalopram" instead, in three places, including, mysteriously, in a "hidden" text box in that graph I showed earlier:

I'm not making this up: I stumbled upon a text box which is invisible, but if you select it with the cursor, you find it contains "escitalopram"! I have no idea what the story behind that is, but at best it is seriously sloppy.

Come on Janssen. Raise your game. In the glory days of dodgy antidepressant research, your rivals were (allegedly) concealing data on suicides and brushing whole studies under the carpet, to make their drugs look better. Despicable, but at least it had a certain grandeur to it.

Bonaventure, P., Dugovic, C., Kramer, M., De Boer, P., Singh, J., Wilson, S., Bertelsen, K., Di, J., Shelton, J., Aluisio, L., Dvorak, L., Fraser, I., Lord, B., Nepomuceno, D., Ahnaou, A., Drinkenburg, W., Chai, W., Dvorak, C., Carruthers, N., Sands, S., and Lovenberg, T. (2012). Translational evaluation of JNJ-18038683, a 5-HT7 receptor antagonist, on REM sleep and in major depressive disorder Journal of Pharmacology and Experimental Therapeutics DOI: 10.1124/jpet.112.193995

Bias in Studies of Antidepressants In Autism

There's little evidence that antidepressants are useful in reducing repetitive behaviors in autism - but there is evidence of bias in the published literature. That's according to Carrasco, Volkmar and Bloch in an important report just out in Pediatrics: Pharmacologic Treatment of Repetitive Behaviors in Autism Spectrum Disorders: Evidence of Publication Bias

They looked at all of the published trials examining whether antidepressant drugs (mostly SSRIs, like Prozac) were better than placebo in reducing repetetive behaviours in children or adults with an autism spectrum disorder (ASD).

A meta-analysis showed that there was a statistically significant benefit of the drugs overall, but it was marginal, with a small effect size d=0.22, and it was driven mainly by two old, very small studies that found big benefits. One of them only had 12 subjects. By far the largest study, King et al (2009) with 149 people, showed zero effect.

This plot shows all of the studies, with the red line being no benefit of drug vs placebo. The further to the right of the line, the bigger the benefit, but the grey horizontal lines show the uncertainty. As you can see, two small, messy studies found big effects, the others didn't.

Worse yet, although there were 5 published studies, the authors also found that there had been 5 studies that had been completed, but never published. Carrasco, Volkmar and Bloch wrote to the people in charge of those studies and asked for data; only one out of 5 replied. The data showed no benefit.

We don't know what the other 4 unpublished studies found, but the way science works means they probably came out negative. If we assume that they did, then even the small benefit seen in the published studies disappears.

This paper, incidentally, is great example of why trial registration is a great thing. Without mandatory pre-registration on clinicaltrials.gov, no-one would know about the 6 unpublished trials at all. It would have been even better if the researchers had been forced to make public the results, as well as the existence, of the unpublished trials; but it's a lot better than nothing.

Finally, the authors of this paper stress that this doesn't mean antidepressants don't help at all in autism - just that they probably don't help with repetitive behaviors.


Carrasco, M., Volkmar, F., and Bloch, M. (2012). Pharmacologic Treatment of Repetitive Behaviors in Autism Spectrum Disorders: Evidence of Publication Bias Pediatrics, 129 (5) DOI: 10.1542/peds.2011-3285

DSM-5: A Little Mix Up

Proposals in the upcoming DSM-5 psychiatric manual for diagnosing "mixed" mood states may be muddled, according to a new paper.

The mixed state - the name alluding to a mix between depression and mania - has traditionally been viewed (more or less) as combining the dysphoria of depression with the energy of mania. Anger, agitation, restlessness and so forth.

I've been depressed and I know only too well the difference between that "active" depression and the "inactive" kind; if I had to choose, I'd always go for the latter, because at least you're in less danger of doing or saying something you later regret.

However, in the proposals for DSM-5, "mixed" episodes as such will be abolished. Instead, a depressive episode will have "mixed features" if it is associated with at least 3 of 7 symptoms normally seen in (hypo)mania. But - and here's the key novelty - those 7 are only the "good" symptoms of mania. Not things like anger, irritability, insomnia or 'aimless' hyperactivity. (Edit: There are also separate criteria for "mixed" manic and hypomanic episodes).

What will this mean? In a new paper, psychiatrists Perlis, Cusin, and Fava tried to find out. The large STAR*D antidepressant trial recruited people with depression, but it gave everyone the Psychiatric Diagnosis Screening Questionnaire (PDSQ), amongst many other measures. This helpfully included six items on "mania symptoms", which correspond pretty closely to the DSM-V proposed "mixed" features.

Perlis et al found that depressed patients who reported experiencing these "mixed" items had a better response to antidepressant treatment. The more mixed symptoms, the more likely they were to get better on the common SSRI citalopram, even adjusting for other variables.

That's the exact opposite of what you'd expect from a measure of "mixed states", as these are thought to be less responsive to antidepressants - maybe even caused by them. There was no placebo group, so it's unclear why they got better, but either way, it's unexpected; the authors declare themselves "surprised". Hmm. What a mystery...

Or maybe not. These manic symptoms are all things that you're not when you're depressed. The 6 items actually make a good summary of what depression, even agitated depression (except maybe #6) isn't.

So, one interpretation of these results is that people who endorsed these items just weren't depressed, at some point in the 6 months prior to doing the PDSQ. Assuming they were depressed at other points that means their mood was variable over time.

People whose depression is variable might well be more likely to recover than the ones whose depression was unrelenting.

Now Perlis et al do consider this -

further models were fit incorporating the IDS-C30 pleasure and reactivity items; results were essentially unchanged indicating that they are unlikely to be confounded by mood variability per se...

But this assumes that the IDS-C30 questionnaire is a good measure of mood variability in this sample. Maybe it's not, and these data are telling us so. I'd have said that's more likely than the idea that these people were actually both cheerful and depressed at the same time, which seems like a contradiction in terms.

Maybe I'm wrong, and these people did feel that, but the problem is, we can't tell, because no-one actually sat down and asked these people what was going on, or heard their account of what they meant by ticking both the "depressed" and "manic" boxes.

Did they experience a strange mixed emotional state in which they simultaneously depressed and happy? Did their mood see-saw from one day to the next? Or weekly, monthly? Were they depressed in the day and happier in the evening? Were they depressed, then back to normal, leading them to see the normal as a 'high', by comparison with the lows? Were they depressed when sober and happy when drunk? Vice versa? Are they experiencing normal ups and downs and interpreting them as 'mood swings' because they've become convinced, for whatever reason, that they have a mood disorder? Did they just have a poor command of English and weren't really trying to say what the highly-educated investigators assume they were?

Who knows? No-one, because no-one asked. Rely on questionnaire 'measures' (as if emotions can be measured) as a replacement for understanding, and you'll end up where this paper does - with a 'result' that's impossible to understand.

Don't seek, and ye shan't find.

It's not great news for the DSM-5 proposals, either way, although defenders could hold out hope that the differences between those criteria and the PDSQ measure might mean the DSM-5 will perform better...

 Perlis, R., Cusin, C., and Fava, M. (2012). Proposed DSM-5 mixed features are associated with greater likelihood of remission in out-patients with major depressive disorder Psychological Medicine, 1-7 DOI: 10.1017/S0033291712000281

Ketamine - Magic Antidepressant, or Expensive Illusion?

Not one but two new papers have appeared from the Carlos Zarate group at NIMH reporting that a single injection of the drug ketamine has rapid, powerful antidepressant effects.

One placebo-controlled study found a benefit in depressed bipolar patients who were already on mood stabilizers. The other found benefits in treatment-resistant major depression, though ketamine wasn't compared to placebo that time. Here's the bipolar trial:

There have now been several studies finding dramatic antidepressant effects of ketamine, a compound that all journalists seem contractually bound to call either a or a "club drug" or a "horse-tranquilizer". Great news?

If you believe it. But hold your, er, horses... there's a problem. As I said almost 3 years ago about one of the earlier ketamine trials:

In theory, the trial was double blind - neither the patients nor the doctors knew whether they were getting ketamine or placebo. But you'll know when you've been injected with 0.5mg/kg ketamine. You get high. That's why people take it [recreationally]. The study can't really be called double blind.

To their credit, Zarate et al did acknowledge this, and suggested that in future ketamine could be compared to another drug which produces noticeable effects. But they really should have done that to begin with.

It's now 2012, and there have still not been any published studies comparing ketamine to an active comparator i.e. a different drug that produces noticable psychoactive effects, to avoid unblinding. This means it's 12 years since the initial pilot report on ketamine in depression, and 6 years since the first large trial appeared.

The authors of the 2006 paper themselves wrote that "limitations in preserving study blind may have biased patient reporting... One potential study design in future studies with ketamine might be to include an active comparator" and suggested amphetamine for the big role.

Good idea. But six years later, we're still waiting. Which is really a bit silly. There have been dozens of papers written about the possible antidepressant effects of ketamine, from human trials to mouse work. That's a lot of research dollars (and dead mice) on something that might just be an active placebo.

Looking at the registered ketamine research on clinicaltrials.gov, I found that four active-comparator ketamine trials are in the pipeline (1,2,3,4), plus one cancelled (5). Only one is for depression though. The others being for OCD, cocaine dependence and suicidal ideation.

In all of these trials a benzodiazepine is the active comparator. Is that a good idea? Well, it's certainly better than nothing, but I wonder.

An active comparator has to "make an impression" on the patient equal to that produced by the real drug.  The null hypothesis, remember, is that ketamine has no specific antidepressant effect. That means it produces improvement through a combination of a) the placebo effect (expectation) and b) non-specific psychoactive changes.

More on that second one: any psychoactive drug might relieve depression by "taking your mind off it" and a change in mental state, as provided by a drug, also provides a demonstration that "I won't always feel this way". By showing that states of consciousness are products of brain chemistry, almost any drug could therefore offer a "glimmer of hope" to the depressed. If all this sounds very subjective, it is, but that's the point. Psychiatry is.

Would a benzo make as big an impression as 0.5 mg/kg ketamine IV? It's impossible to predict, really; so we'd need to ask people about the subjective strength of the drug effect. Personally, I worry that a lot of people just get sleepy on benzos and don't really feel much, so I'd prefer they used something a bit more hard-hitting like amphetamine, but maybe that's just me.

There's a deeper problem though. Suppose our ketamine-benzo trial finds no difference between ketamine and benzo. A critic could say, ah, but maybe it was just a "failed trial", so it doesn't overturn the positive studies. The patients weren't properly diagnosed, or weren't depressed enough, or were too depressed, etc.

Nitpicking such differences between studies is a well-practiced art.

Critics could complain in other ways if the study did find a benefit of ketamine. As I see it, the only way to settle this once and for all is to do a three-way randomized controlled trial - inactive placebo vs. active comparator vs. ketamine.

That way, if it's a failed trial, we'd know: there'd be no difference between ketamine and the inactive placebo. If there was a difference, but the active comparator was just as good as ketamine, that means it was all about nonspecific effets. Finally, if ketamine was better than the other two conditions, we could be pretty confident it was really working.

Also important is the question of volunteer expertise; subjects shouldn't be able to tell what drug they're on, but people who'd taken ketamine and/or the comparator drug before might be able to do that, so you'd want naive volunteers.

In conclusion: It's possible that ketamine has no specific antidepressant effects. To find out we ideally need a three-way trial, with both active and inactive comparators, careful monitoring of subjective drug effects and patient knowledge and expectations. Until that happens, I will be skeptical of ketamine in depression.

This is not because I just think it's impossible. Ketamine profoundly affects the brain in ways that we don't understand. I've suffered depression and I know it can come and go in a matter of minutes. So I think it's entirely possible that it works - but it's also possible that it's a nonspecific effect.

Look. I really want to know the answer to this. Both as a neuroscientist, and as a depression sufferer, this is very important to me. That's why we urgently need a good trial.

Link: See also the discussion and the comments over at The Neurocritic and this Scientific American piece which is pretty good except that it doesn't cover the active placebo issue.

Zarate CA Jr, Brutsche NE, Ibrahim L, Franco-Chaves J, Diazgranados N, Cravchik A, Selter J, Marquardt CA, Liberty V, and Luckenbaugh DA (2012). Replication of Ketamine's Antidepressant Efficacy in Bipolar Depression: A Randomized Controlled Add-On Trial. Biological psychiatry PMID: 22297150

Ibrahim, L., et al. (2012). Course of Improvement in Depressive Symptoms to a Single Intravenous Infusion of Ketamine vs Add-on Riluzole: Results from a 4-Week, Double-Blind, Placebo-Controlled Study Neuropsychopharmacology DOI: 10.1038/npp.2011.338

Psychiatry's True Blood? Pt 1.

Imagine that there was a blood test that could detect depression. Wouldn't that be useful?

It depends.

Ridge Diagnostics are a US company who offer such a test. They've just published some results of the technology in Molecular Psychiatry. In two samples of patients with major depressive disorder (MDD), they report differences in the "MDDScore", between the patients and healthy controls.

The MDDScore is an aggregate value, calculated from the levels of 9 metabolites in blood serum. They're all well-known molecules, including hormones, such as cortisol and prolactin. The novelty is in how they're put together to make the MDDScore. We're given equations - but the key variables are not provided, because they're proprietary:

Long-term Neuroskeptic readers will recall that this "secret ingredients" approach to publishing science was also adopted by another company offering a different depression test.

Anyway, the performance of the test was impressive. In both the pilot and the replication samples, the MDDScore was significantly higher in the depressed people than in the controls. In both cases, the test had a sensitivity of over 91% and a specificity of over 81%, which is pretty good. Ridge Diagnostics are already offering the MDDScore clinically. For $745 a pop.

However...

Although there were two depressed patient groups (n=36 and 34), there was only one set of controls (n=43); both patient samples were compared to it. This means the second, "replication", test was not fully independent of the first one. If the first finding was a fluke caused by the control group having weird results by chance, for instance, then the second study would just repeat the fluke.

The patients were significantly older, and with a higher BMI, than the controls. They did control for these variables, which is good, but this raises the question of whether these folks differed in other ways, that they didn't measure, and hence couldn't control for.

In both samples, the patients had a very significantly higher MDDScore than the controls (p less than 0.0001, both times). But in both cases, the difference in levels of EGF (epidermal growth factor) was almost as strong: p=0.0003 and p less than 0.0001, respectively. Other metabolites weren't far behind. Testing for EGF would almost certainly be cheaper than getting an MDDScore.

Finally, all these data demonstrate is that the test can distinguish between people with MDD and entirely healthy people. But how often are doctors going to need to do that? More likely, they'll want to distinguish depression from other things that are often confused with it, such as: bipolar disorder, anxiety disorders, chronic fatigue syndrome, bereavement, "stress", and all manner of physical illnesses e.g. thyroid problems. Daniel Carlat said last year that

If the test cannot distinguish different psychiatric problems, then the MDDScore is simply a non-specific "biomarker" for emotional difficulties of all stripes, and would be essentially useless.

How disorder-specific is the MDDScore? This paper doesn't tell us. And to date, this is the only published paper mentioning the MDDScore. The website mentions some conference presentations, but none have yet appeared in a peer reviewed journal.

Ridge Diagnostics have an interesting history. But that's another story - stay tuned for Part 2.

Papakostas, G., Shelton, R., Kinrys, G., Henry, M., Bakow, B., Lipkin, S., Pi, B., Thurmond, L., and Bilello, J. (2011). Assessment of a multi-assay, serum-based biological diagnostic test for major depressive disorder: a Pilot and Replication Study Molecular Psychiatry DOI: 10.1038/mp.2011.166