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

Neither Drugs Nor Therapy Prevent Psychosis

Neither medication nor psychotherapy is effective in improving the prognosis for youngsters considered to be at high risk of developing psychosis, according to a major study just published.

The idea of identifying and treating young people at risk of becoming psychotic - because of a family history of schizophrenia, or because they're showing some mild symptoms - has become very fashionable lately. But can we really do anything to pre-empt the disorder?

In this trial, 115 "ultra-high risk" Australian subjects were randomized to three different treatment conditions, or if they didn't agree to treatment, they were just followed up to see what happened.

The treatments didn't work. Here's the smoking gun, showing the proportion who didn't go psychotic over time:

This shows all four of the subject groups did pretty much the same in terms of their likelihood of becoming psychotic. Neither cognitive therapy, nor the antipsychotic drug risperidone (at a low dose) had any effect: those given 'supportive therapy' (basically: sympathetic chats) and a placebo pill did just as well.

There probably wasn't even a placebo effect: none of the three treatment groups did better than people who got no treatment at all (monitoring group), although people weren't randomly assigned to that group, so that's a little less clear.

Is this a surprise? Yes, if you believed the early studies to examine this question which claimed great things for drugs and therapy. But the current findings are no shock if you've been following the (much larger) recent trials - for example the British one from earlier in the year, which found zero benefit of cognitive therapy.

Early small trials have a nasty habit of not working out in the long run.

The other lesson here is that even "ultra-high risk" folks usually don't get psychotic: only about 10-20% of them, in fact, became ill in the first two years of this study; the British results I mentioned are very similar.

So is this really "ultra high"? Relatively, yes it is; even a 10% risk is far higher than the chance that a random person on the street would have. But in absolute terms, perhaps not.

A concern here is that rounding these folks up, labelling and 'treating' them might make their lives worse, or even increase the risk of psychosis. That's not just my opinion: that's what the very cognitive therapists who eagerly run these trials believe (or ought to, if they're being consistent with their own theories).

One of the key ideas in cognitive accounts of psychosis is that the belief and fear that one is 'going crazy', or that you're otherwise abnormal, is itself a major source of stress that actually leads to worsening of symptoms.

What could be scarier than being told you're at "ultra high risk"?

Preventing psychosis is a great idea in theory. But most bad ideas are.

McGorry, P., Nelson, B., Phillips, L., Yuen, H., Francey, S., Thampi, A., Berger, G., Amminger, G., Simmons, M., Kelly, D., Thompson, A., and Yung, A. (2012). Randomized Controlled Trial of Interventions for Young People at Ultra-High Risk of Psychosis The Journal of Clinical Psychiatry DOI: 10.4088/JCP.12m07785

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

A New Theory of Psychosis?

A team of British neuroscientists led by the (in)famous David Nutt says that magic mushrooms offer a new theory of psychosis: Functional Connectivity Measures After Psilocybin Inform a Novel Hypothesis of Early Psychosis

It's a reanalysis of a study from earlier this year, which got quite a lot of attention, in which 15 volunteers were injected with psilocybin - the major active hallucinogenic ingredient in 'magic mushrooms' - during an fMRI scan.

In a nutshell, the rather interesting proposal in the new paper is that psilocybin may cause mind-altering effects by blurring the difference between the brain networks responsible for 'internal' and 'external' thought.

Activity in the internal "default mode network" (DMN) is generally anti-correlated with the "task-positive network" (TPN) - when one is higher, the other's lower. The DMN is active when you're not doing much - hence 'default' while the TPN comes online when you're engaged in a particular mental activity.

Nutt's team say, however, that their functional connectivity fMRI data show that after psilocybin, activity in these two networks becomes positively correlated - an unusual pattern. They write:

Increased DMN-TPN coupling has been found in people at high risk of psychosis and an inability to distinguish between one’s internal world and the external environment, sometimes referred to as “disturbed ego boundaries,” is a hallmark of early psychoses and the psychedelic state.

One of our volunteers reported the following after psilocybin: “It was quite difficult at times to know where I ended and where I melted into everything around me.”

To be honest I'd need to see a replication before I put too much faith in this, because this kind of post-hoc reanalysis of fMRI data is very flexible and therefore prone to false positives, but it's an interesting idea, and at least it provides a clear theory for further research.

Carhart-Harris RL, Leech R, Erritzoe D, Williams TM, Stone JM, Evans J, Sharp DJ, Feilding A, Wise RG, and Nutt DJ (2012). Functional Connectivity Measures After Psilocybin Inform a Novel Hypothesis of Early Psychosis. Schizophrenia bulletin PMID: 23044373

Cocktail-Party Neuroscience

"That's all very well, but what about the real world?"

This, or something to this effect, is a stock criticism of much of psychology and cognitive neuroscience. Studies of human behavior and brain function under carefully controlled laboratory conditions don't tell us much about everyday life, the argument goes.

It's a serious point. But a group of neuroscientists have now sought to dispel such worries in rather spectacular fashion. With the help of some nifty wireless headsets, Alan Gevins and colleagues of San Francisco took electroencephalography (EEG) out of the lab and organized an EEG party - allowing them to record brain electrical activity from 10 people as they chatted and drank vodka martinis. An electroencephalorgy one might say.

This is perhaps the only time in history that scientists have admitted, on record, to getting drunk with their research funding.

Pics or it didn't happen? They have pics:

And more:

The odd device held by the girl in blue is an alcohol breathalyser, which brings us onto the purpose of the study, which was to measure the effect of alcohol on brain activity.

The authors first measured the effect of alcohol on brain alpha, beta and theta band activity under standard lab conditions, and then checked to see if the results translated to the party. They did, surprisingly well in fact (although the whole thing relied on a multivariate model of the kind that make purists suspicious.)

Still, only 40% of the party data was deemed unusable due to electrical artifacts caused by participants speaking, swallowing, chewing and so forth, which is pretty good, and suggests that real-world EEG could be much more feasible than many neuroscientists would have predicted (given how annoying these sources of noise can be even under lab conditions I'd have guessed it would be more like 90%).

Now I'll make an admission: when I first read this paper, I was cynical. I felt sure it was some kind of advert for the authors' products, probably the nifty wireless EEG caps they used. "Oh very clever," I thought. "You run a wacky study, it goes viral, and you get free advertising. Well, it's worked on me, but I'm going to call you out on it."

However, the authors were one step ahead, because the paper assures readers that:

The authors are employed by the San Francisco Brain Research Institute and SAM Technology which are 100% supported by competing research grants from the U.S. Federal Government... The organization only performs research and offers no services or products. None of the authors perform consulting work. It is very unlikely that any corporation, investor, etc. would find it commercially worthwhile to buy or license the technologies that the authors have made to do their research.

OK then.

Gevins A, Chan CS, and Sam-Vargas L (2012). Towards measuring brain function on groups of people in the real world. PloS one, 7 (9) PMID: 22957099

A Bloody Mess: Pharma, Legal Threats, and Fraud

Over at ScienceInsider, we read that a German pharma company, Fresenius Kabi, threatened a scientist with legal action over a paper published in the New England Journal of Medicine.

The paper asked, in effect: what's the best way to boost blood volume after bleeding? The old-fashioned - and cheap - approach is to give water with various salts, called Ringer's solution. However, it has been proposed that it might be more effective to add a form of starch to the mix, specifically hydroxyethyl starch (HES).

In essence, just as you can use starch to thicken a soup, HES helps to bulk out the blood, increasing the volume, to better compensate for fluid loss. However, HES carries the risk of side effects, including severe kidney damage.

Do the benefits outweigh the risks? That was the question asked by a team of researchers led by Danish Dr Anders Perner. In a double blind, randomized controlled trial, Perner and colleagues compared a particular kind of HES (6% HES 130/0.42) to Ringer's solution, in patients with severe sepsis (blood poisoning) treated in intensive care.

The results showed that HES was actively harmful. It raised the risk of death in these severely ill patients. 51% died, compared to 43% in the control group:

Phew! Glad we know that. If you ever end up in intensive care with sepsis, this paper could well have improved your chances of survival.

Here's where the legal threats came in. When Perner et al published their work, they described it as a trial of 6% HES 130/0.4. It was in fact a trial of 6% HES 130/0.42. Spot the difference? Fresenius Kabi did, and they weren't happy, because they sell the 130/0.4 product. The trial was, incorrectly, billed as being about their product. It was in fact about a very similar product.

And they really are very similar. The 0.4/0.42 refers to the average hydroxylethyl ratio of the starch. But this is only an average - it varies from molecule to molecule. At ScienceInsider, Perner points out that the ratio varies between 0.40 to 0.44 in the "0.42" brand, and 0.38 to 0.45 in Fresenius Kabi's "0.4".

That's a lot of overlap... 100% overlap actually. Still, a mistake is a mistake, so Perner was right to correct it, but why couldn't they just have asked nicely?

Well... maybe because it's not the first controversy involving Fresenius Kabi and their starchy solutions. In fact, they're linked to one of the biggest scientific scandals in recent years: the case of Dr Joachim Boldt. Boldt was one of the leading researchers in his field, until last year when it was revealed that much of his work was fraudulent, unethical, or both. He's since been made to retract over 90 of his papers - which at one time made him the most-retracted scientist ever.

Now Boldt's main research interest was... hydroxyethyl starch. Much of his work - including many of the retracted papers - seemed to show that HES was both safe and effective, and he received funding from Fresenius Kabi.


So, the fall of Boldt must have deal FresKab a bit of a blow. They developed HES, back in the 1970s, and now the star cheerleader for their invention has been revealed as one of the biggest medical fraud in history. It's not hard to see why they might be feeling especially sensitive right now.

Sure, Boldt received funding from other companies too, and FresKab funded plenty of other researchers too. There's no reason to believe that they were aware of Boldt's misconduct, or that they encouraged it. But indirectly they almost certainly did benefit from it.

Anyway, following the legal threats, the NEJM has now corrected the Perner study. It was not a study of Fresenius Kabi's product. Rather, it was a study of a very similar product, and it showed that this very similar product kills people. So spread the word!

Perner A, & et al (2012). Hydroxyethyl starch 130/0.42 versus Ringer's acetate in severe sepsis. The New England journal of medicine, 367 (2), 124-34 PMID: 22738085

On Twitter, It's Beer Before Liquor

People tweet about beer in the evenings, especially on Fridays, according to a not-very-surprising-but-still-fun little report in the journal Epidemiology: Using Twitter to Measure Behavior Patterns

The study used timeu.se, a free searchable database of millions of Tweets. The site grew out of an excellent bit of research you might remember from last year that examined how average mood varies over the course of the day and year.

People tweet about and presumably drink beer (and wine) most in the evenings, especially on Fridays and Saturdays. Smoking-related tweets however were mostly flat, although there did seem to be a small peak in the mornings.

So I ran a few searches of my own, and I noticed that different drinks peak at different times. "Beer" is most popular in the early evening, closely followed by "Wine", but "Vodka" doesn't max out until midnight.

Looks like people are not following the old "beer before liquor, never sicker" rule.

Also, while wine gets the most tweets during the week, beer and vodka really take off at the weekend.

 Cunningham A. John (2012). Using Twitter to Measure Behavior Patterns Epidemiology DOI: 10.1097/EDE.0b013e3182625e5d

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.

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

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

Beware Reverse Publication Bias

In all the fuss over the pressure for scientists to publish positive results, we may have been missing an equally dangerous kind of publication bias operating in the opposite direction.

So say Luijendijk and Koolman in the Journal of Clinical Epidemiology: The incentive to publish negative studies: how beta-blockers and depression got stuck in the publication cycle.

The background here is the possible link between beta blockers and depression. Beta blockers are drugs widely used to treat high blood pressure. Some studies have reported that they raise the risk of depression, though many others found no link. Propranolol is said by some to be the worst offender because it's best at entering the brain.

Luijendijk and Koolman say that beta blocker-depression studies have appeared in the form of "publication cycles" - first a positive study appears, and then negative ones follow. Then another study finds a positive link using a different method - and rebuttals, using those methods, soon appear. They sketch out several such positive-negative cycles based on different methods and particular hypotheses.

Now, there's two ways to look at this. You could explain this in terms of standard positive publication bias. Maybe lots of people looked into a possible link, the ones who found nothing didn't publish. Then someone, by chance, did find an association with depression, and they published it. Once that happens, the question became a hot topic so the unpublished negative studies were dusted off and submitted.

But there's a more worrying possibility. What if the original positive studies were correct, and the subsequent negative studies were the product of an inverse publication bias in favor of contrarian negative results?

The publication cycles in the literature about beta-blockers and depression seem to suggest that
the very publication of positive studies, whether true or false, increases the incentive to publish negative results, whether true or false... [in the case in question] the first as well as a significant number of subsequent negative studies were published in high-impact journals (8 of 19 journals with 2009 impact factor greater than 4.0). Third, power analysis showed thatd in two cycles, the first negative studies were underpowered...

If a true-positive study stimulated the publication of one or more false-negative studies, again an invalid picture of the true association would emerge. Publication of false-negative studies may thus give rise to publication bias, just like publication of false-positive studies. Research groups usually compete to get the first positive study published in a high-impact journal. It has been suggested that it could also be worthwhile to aim at getting the first study that challenges the former published.

This is not an entirely new idea. It was described in the classic Why Most Published Research Findings Are False, but only in passing.

To be honest it's impossible to know, in any particular case, whether inverse publication bias is at work. Depending upon whether you think beta blockers cause depression (and that's still controversial), your interpretation of the biases in the literature will probably differ.

However, I think the basic idea is important. Publication bias isn't a bias in favor of positive results per se. It's a bias towards "interesting" results - which in most cases means positive ones, but could equally well include negative ones, in certain contexts. In some ways, this could be a good thing, if the negative and positive biases eventually cancelled out, leaving a neutral playing field; but there's no guarantee that would ever happen.

As for how to fix publication bias - my opinions on that question are well known...

Luijendijk, H., and Koolman, X. (2012). The incentive to publish negative studies: how beta-blockers and depression got stuck in the publication cycle Journal of Clinical Epidemiology DOI: 10.1016/j.jclinepi.2011.06.022

The Trojan Horses of Medicine

Dodgy science is being smuggled into medical journals thanks to a loophole in the regulations, say Italian psychiatrists Barbui and Cipriani in an important article.

They focus on agomelatine, a recently-approved antidepressant. But their point applies to all of medicine, not just psychiatry.

Here's the problem. Nowadays, major medical journals have rules governing systematic reviews and meta-analyses of clinical trial data. If you want to review the evidence about how well a certain drug works, or its safety, you've got to do it properly. You have to consider all of the data, not just focus on the results that suit you. And so on.

However, these rules don't apply to "narrative" review papers, which is a broad term meaning any kind of article meant to give a discussion of the pharmacology, history, chemistry etc. behind a particular drug. For a narrative review, there are no rules.

In particular, you can write about the clinical trial data in such articles with no restrictions. Unlike in a proper systematic review, you can cherry-pick trials and so on to your heart's content. Some narrative reviews have so much clinical data in them that they end up being, in effect, a bad systematic review. One that would never have been deemed acceptable as a systematic review.

Barbui and Cipriani argue that narrative reviews are often used in this way, namely to paint drugs in a positive light. In the case of agomelatine, they mention a number of recent narrative reviews which were supposedly about the drug's mechanism of action, but which actually contained extensive (but biased) reviews of the clinical trial data.

It's not hard to see how pharmaceutical companies might take advantage of this process.

However, the problem is surely not limited to agomelatine. It's a loophole that affects every branch of medicine:

Most medical journals require adherence to the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA). It is an evidence-based minimum set of items for reporting in systematic reviews and meta-analyses. Adherence to PRISMA is not required in review articles dealing with basic science issues as these articles are not focused on clinical trials.

In practice, however, the agomelatine case indicates that clinical data are regularly included and reviewed with no reference to the rigorous requirements of the PRISMA approach. These articles have this way became a modern Trojan horse for reintroducing the brave old world of narrative-based medicine into medical journals.

How do we stop this? It's simple, the authors say: just make all references to clinical data subject to PRISMA, or other accepted regulations, whatever the supposed 'primary focus' of the paper:

We argue that medical journals should urgently apply this higher standard of reporting, which is already available, easy to implement and inexpensive, to any form of clinical data presentation.

Of course, there are plenty of good narrative reviews that really do cover the pharmacology or other science in a useful way. The problem is not narrative reviews as such, but the way they're used.

Barbui, C., and Cipriani, A. (2012). Agomelatine and the brave old world of narrative-based medicine Evidence-Based Mental Health, 15 (1), 2-3 DOI: 10.1136/ebmh.2011.100485

Challenging the Antidepressant Severity Dogma?

Regular readers will be familiar with the idea that "antidepressants only work in severe depression".

A number of recent studies have shown this. I've noted some important questions over how we ought to define "severe" in this context, and see the comments here for some other caveats, but I'm not aware of any studies that directly contradict this idea.

Until now. A new paper has just come out which seeks to challenge this dogma - not the author's term, but I think it's fair to say that the severity theory is becoming a dogma, even if it's an evidence-based one (but then, all dogmas start out seeming reasonable).

However, while the new paper is interesting, I think the dogma survives intact.

The authors went through the archives of all of the trials of antidepressants for depressive disorders conducted at the famous New York State Psychiatric Institute for the past 30 years. They excluded any patients who were severely depressed, and just looked at the milder cases. The drugs were mostly the older tricyclic antidepressants.

With a mean HAMD17 score of about 14, the patients they looked at were certainly mild. By comparison, most trials today have a mean of well over 20, and according to the main studies supporting the severity dogma, you need a score of about 25ish to benefit substantially:

So what happened? They reanalyzed 6 trials with over 800 patients. Overall there was a highly significant effect of antidepressants over placebo in mild depression, with an effect size d=0.52, or about 3.5 HAMD points. This is actually better than most other studies have found in "severe" depression. If valid, these results would torpedo the severity theory.

This seems very interesting... but. There's a big but (I cannot lie). Although the authors say they wanted to include all the relevant trials from the NYSPI, they only had access to the data from 6. There were another 6 projects, but they were "pharmaceutical company studies from which data were not released to the investigators."

This pretty much wrecks the whole deal. If those 6 studies all found no benefit of the drug, the overall average results would be much less impressive. We have no way of knowing what those studies found, but I'd wager that most of them were negative, because of publication bias - we know that drug companies tend to publish positive studies and bury negative ones. Or at least they did, at the time these studies took place (there are better regulations now).

By contrast, severity dogma classic Kirsch et al (2008) avoided publication bias by looking at unpublished data. Fournier et al (2010), the other major severity study, didn't but the data were very similar to Kirsch et al so it's not hard to believe them.

So in my view, until we know what happened in the other 6 trials, we can't really interpret these results, and the severity theory stands.

Stewart, J., Deliyannides, D., Hellerstein, D., McGrath, P., and Stewart, J. (2011). Can People With Nonsevere Major Depression Benefit From Antidepressant Medication? The Journal of Clinical Psychiatry DOI: 10.4088/JCP.10m06760

The Real Story On That "Antidepressant Surge"

Remember last week's story about how depression rates are soaring in Britain? It was all triggered by "new data" about an increase in antidepressant prescriptions.

At the time I was skeptical, not least because the data wasn't actually new, but I've done a bit more digging and it turns out the media coverage was even more misleading than I thought.

Here's some pretty graphs from the NHS Information Centre. I reiterate that all of these are freely available and have been for ages. Here's the one for antidepressants:

They've been rising strongly! In total prescription rates are about 60% higher now compared to in 2006. Oh dear.

What the papers didn't tell you is that pretty much every other class of drug has also increased over that period, by even more in some cases. Here's ADHD drugs, and dementia pills, which have increased by about 75% and 100% respectively:

There have also been steady increases in anticonvulsants and a 40% increase in meds for Parkinson's disease. All of the graphs are here.

So this suggests that there's been a general increase in prescriptions for brain drugs. But in fact it's even wider than that because if we look at the same data for cardiovascular system drugs, we find the same picture for most (although not all) kinds of these medications.

And for painkillers, we find over 50% increases in prescriptions of the stronger opioid drugs, a 20% increase in migraine drugs etc etc. I swear I'm not just copying and pasting the same graph.

Now clearly, all of these increased prescriptions don't mean that there are simultaneous explosions in rates of dementia, heart disease, pain, migraine, Parkinson's and ADHD, all in the past 5 years. We would have noticed if that were the case.

What's happened, clearly, is that doctors are just writing more prescriptions nowadays.

So it's misleading to say that there's been a spike in antidepressant prescriptions. Yes it's technically true but it ignores the context. The truth is that we seem to be experiencing a cultural shift in our relationship to medications - perhaps evidence of the creeping medicalization of life (although there are more prosaic explanations that need to be ruled out before we conclude that; this could be a bureaucratic change in the way prescriptions are counted.)

However, "Escalating Depression Crisis - Antidepressant Use Soars" is a better headline than "Possible Medicalization Gradually Continues For Sixth Year In Row".

The truth, sadly, has an inherent disadvantage in the battle for news coverage. If we find the truth boring, it's easy for someone to come along and make up something attention grabbing. But the only easy way to make the truth more interesting is to make it, well, less true.