Britain - the Prozac Nation? Not So Fast...

Oh no! The stress of the recession has turned us into a nation of antidepressant addicts, according to every single British newspaper this morning.

The media coverage has been predictable with lots of scary, context-free statistics, and boilerplate quotes from the usual suspects. No doubt tomorrow we'll see a selection of moralistic op-eds about this.

But not one of the many nigh-identical articles provided a link to the original data, or even a useful description of where one might find it. After contacting one of the NHS organizations named as the source, I managed to track the numbers down.

It turns out that the key figures have been publicly available since April 2011, so I'm not sure why this story appeared in British "news"papers at all. Also, it would have been easy for journalists to link to the source, if they respected the intelligence of their readers enough to do that. I just did it and it wasn't terribly hard to click "Add Link".

On that note, I actually read a bizarre article today criticizing British journalists for providing too many links to their source data... if only.

Anyway, the data. Ben Goldacre has already written an excellent piece on this (in fact, he wrote it back in April 2011, curiously enough...see above), but here's some more detail.

First off, the data are all about antidepressants, not depression. A crucial distinction, there, because nowadays, antidepressants are widely used for all kinds of other things. Everything from other psychiatric disorders like anxiety and OCD, to non-psychiatric stuff like back and joint pain, premature ejaculation, and menopausal hot flushes.

We can't tell how much of the antidepressant use was for depression. But there are clues suggesting that a lot of it wasn't. It turns out that the second most popular antidepressant (after citalopram) was the very old drug amitriptyline, with nearly 9 million prescriptions per year - or 20% of the total.

Nowadays amitriptyline is rarely used for depression, because newer, less toxic alternatives are available. However it is used, in low doses, to treat chronic pain. So I suspect that pain accounts for a large % of amitriptyline use. That would also explain why the cost to the NHS per prescription of amitryptiline was by far the lowest of all antidepressants: low doses are cheap.

How about the increase over time?

The newspapers are correct that antidepressant use rose from 33.9 million prescriptions in the year 2007/8, to 43 million in 2010/2011. That's a 28% rise over 3 years. However, if we go 3 years further back to the equivalent 2004/5 Prescription Cost Analysis, we find that antidepressant prescriptions were 28.9 million. So they rose 17% in the 3 years before 2007/8, long before the recession was on the horizon.

The recent 28% rise, in other words, is unlikely to be related to the recession, at least not entirely.

We also know(1,2) that the number of antidepressant prescriptions per person has been rising over the past several years in the UK. So the increase in prescriptions might not even mean more antidepressant users - it might just mean that the same number of users are using more each. (And that could mean anything, including that bureaucracies are saving money by prescribing for shorter periods).

One study found that there was no increase in the number of people taking antidepressants for depression from 1993 to 2005, with all of the rise in prescriptions over that period being a product of more prescriptions per person.

Another study did find a true rise in users from 1995 to 2007, albeit lower than the raw figures would suggest, but those figures were limited to a particular part of Scotland and it wasn't just about depression - it included all other uses of these drugs as well.

Overall, it's just impossible to know, from these data, whether there's been a true increase in antidepressant use for depression in recent years. The most we can say is that there might have been one, and if so it might have something to do with the economy.

How Realistic is fMRI?

How representative are fMRI experiments? Is "the brain" that we investigate with fMRI the same brain that we use outside the MRI scanner?

A new paper from Bernhard Hommel and colleagues of Leiden in the Netherlands offers some important caveats. They looked to see what effect playing some recorded MRI scanner sounds had on people's ability to perform some simple cognitive tasks, while sitting outside the scanner.

MRI is notoriously noisy. When you have an MRI scan you have to wear earplugs to protect against the sound but they only block out some of it. Opinions differ on whether the sound is pleasant or not. Personally I find the repetitive tick-tock rather soothing now, but then I've heard it many times over the years. First-timers can find it quite overwhelming.

Anyway, Hommel et al found that while scanner noise had no overall effects on reaction time or accuracy, it actually improved performance on three measures of "cognitive control".

For instance in a task in which participants had to respond to the colour of a circle by pressing the left or the right arrow key, they were slower to react when the circle appeared on the "wrong" side of the screen, i.e. on the left when the correct answer was the right arrow. This slowing of responses caused by a stimulus-response clash is called the Simon effect.

The results showed that the Simon effect was reduced by noise. The same thing happened in two other studies: noise meant better performance.

All of the noise effects were modest and the sample sizes were also quite small (14-18 per task, with everyone studied twice, noisy vs silent) but this paper joins a number of others raising questions about the representativeness of fMRI, with evidence that fMRI activates the brain and maybe even improves mood (although I doubt that last one).

The authors' interpretation is that the noise made people pay more attention to the tasks, to compensate for the distraction, and that this means that fMRI studies may be biased in their measurements of cognitive control:

Generalizing from fMRI findings to behavioral observations and vice versa seems to be more problematic than commonly thought, at least as far as control  processes are concerned. In a sense, then, investigating cognitive processes by means of  fMRI... is inevitably facing Heisenberg’s (1927) uncertainty principle, according to which the act of measurement can change what is being measured.

To my mind the biggest weakness of this is that it only looked at noise. While scanners are noisy, that's not the only distracting thing about them: during an fMRI study you also have to lie down, in a small confined tube, and your only way to see the "screen" on which experimental stimuli are shown is indirectly via a small mirror which often doesn't give a good view.

So ironically, I'm not sure how realistic this study is...


Hommel, B., Fischer, R., Colzato, L., van den Wildenberg, W. and Cellini, C. (2011). The effect of fMRI (noise) on cognitive control. Journal of Experimental Psychology: Human Perception and Performance DOI: 10.1037/a0026353

Scanning The Brain While Looking At Scans

A new study investigated what goes on in the brain when doctors make a diagnosis.

Radiologists use X-rays and other imaging techniques to diagnose diseases - but in this study, they went into the scanner themselves. Brazilian researchers Marcio Melo et al used fMRI to record neural activity while the radiologists were shown an array of chest X-rays.

Some of the scans showed evidence of disease, which the doctors were required to diagnose. There were also two control conditions, in which the stimuli were still X-rays but with little pictures of either animals or letters embedded in them, instead of diseases.

The image above shows how it worked. As well as pneumonia, one patient has a severe case of Alligator Lung, while the other looks like they've got the Influenza 'B' virus.

Now, the point of all this was to compare the mental process of making a diagnosis to that of seeing an object. The idea is that a trained radiologist sees particular diseases in the scans, in the same way that anyone can see an alligator.

Activity during diagnosis, object-recognition and letter naming was very similar (compared to doing nothing); this presumably represents the visual and language areas involved in looking at the image, recognizing what it is, and saying it out loud:

There were some slight differences, with the left inferior frontal cortex and the posterior cingulate cortex being more activated by diagnosis than animals. But this difference disappeared after controlling for the number of different possible descriptions the radiologists reported thinking about for each image.

The authors conclude that

These results support the hypothesis that medical diagnoses based on prompt visual recognition of clinical signs and naming in everyday life are supported by similar brain systems.

Which seems fair enough, although it's important to remember that the diagnoses in this study were quite easy ones. The mean response time was just 1.3 seconds and only 6% of those split-second diagnoses were wrong. Unfortunately diagnosis is not always that easy.

Anyway, this study is all very well, but why stop at chest X-rays? Last year I speculated on the fun neuroscientists could have with a real-time fMRI machine:

You could lie there in the scanner and watch your brain light up. Then you could watch your brain light up some more in response to seeing your brain light up...

We really need to scan people while they're looking at brain scans. Only then will we be able to understand the neurological basis of being a neurologist, and find the brain's looking-at-a-blob blob.

Melo M, Scarpin DJ, Amaro E Jr, Passos RB, Sato JR, Friston KJ, and Price CJ (2011). How doctors generate diagnostic hypotheses: a study of radiological diagnosis with functional magnetic resonance imaging. PloS ONE, 6 (12) PMID: 22194902

Neuroskeptic: The Video Game

As a Christmas present, here's something I've been working on over the holidays - Neurubiks.

It's a free puzzle game. The brain is broken. Can you can restore neuro-harmony?

Download it here.

Features:

• A bit like a Rubik's cube, but less annoying. 
• Millions of possible puzzles.
• Easy to learn - just click on the blobs.
• Neuroanatomically accurate.
• Perfect for killing time while running fMRI analyses.

Notes:

If you like it, hate it, find bugs or have any suggestions, please let me know in the comments.

If I knew Flash, I would have programmed this in Flash. If any Flash developers like Neurubiks and are interesting in helping develop it please do get in touch.

Apologies to the color-blind. The game is all about colours I'm afraid. Let me know if you have any ideas for making it more color-blind-friendly.

An Objective Measure of Consciousness...?

Could a puff of air in the eye offer a way to evaluate whether someone is conscious or not?

Yes it could, say Cambridge's Tristan Bekinschtein and colleagues in a new paper about Sea slugs, subliminal pictures, and vegetative state patients.

It's all about classical conditioning of the kind made famous by Pavlov. This is learning caused by the pairing of two stimuli, one of them somehow meaningful (usually unpleasant). So if I were to ring a little bell before, say, pepper spraying you, and I did that repeatedly, you would probably close your eyes whenever I rang that bell. Or just punch me, but you see the point.

Anyway, the key is that there are two kinds of classical conditioning. In the unhelpfully named "delay" conditioning, the warning stimulus overlaps with the painful one. Like if I started ringing my bell, then kept ringing it while I sprayed you with my other hand. In other words, there is no delay between the two stimuli... I said it was badly named.

By contrast in "trace", conditioning there is a delay - the warning stops shortly before the second stimulus. Bekinschtein et al argue that trace conditioning requires conciousness. While delay conditioning can occur without awareness of the link between the two stimuli, only conscious awareness can bridge the time gap in trace conditioning.

In trace experiments (in which rather than pepper spray, the unpleasant stimulus is just a puff of air in the eye), people who, when asked, can't explain the relationship ("sound means puff") don't learn to blink when they hear the sound. But with delay conditioning, this "unconscious" conditioning can occur. Likewise, under anaesthesia, trace conditioning is lost.

At first glance this looks like a piece of psychological trivia, but it could have literally life-or-death consequences. If trace conditioning is a measure of concious awareness then it could be used as a way of working out whether brain-injured people in a "coma" or "vegetative state" are aware or not.

This paper is in fact a follow-up to the author's own 2009 study showing that some people in a vegetative state do show trace conditioning - and the ones who did were more likely to subsequently wake up.

One snag is that the humble sea slug, Aplysia, can undergo trace conditioning, yet it is presumably not conscious, at least not in any recognizable sense.

But Bekinschtein et al say that trace conditioning is a product of convergent evolution. Alplysia can do it and we can do it, but we use different means to the same end. Their argument is that while in Alpysia trace conditioning is known to be dependent on just a handful of individual neurons in the creature's tiny "brain", in humans it requires an intact hippocampus (containing millions of cells). People with hippocampal damage, who suffer amnesia, also can't do trace conditioning.

That's a good point but does that mean such hippocampal patients aren't conscious? That would be weird because, apart from the amnesia, they seem perfectly normal. Presumably they're just not conscious of the relationship between things separated in time...

Also, primitive pathways for conditioning might still exist in humans, able to reactivate under special conditions. They do acknowledge this with a discussion of experiments showing that trace conditioning in the absence of conscious awareness of the relationship can occur but only when the warning stimuli are "scary", like pictures of snakes. They say that with generic, neutral stimuli there is no good evidence of unconscious trace conditioning, but this seems like a fairly fine distinction.


Ultimately, it's a very nice idea but only more studies on "unconscious" patients will tell us whether it's really able to measure consciousness in a useful way.

Bekinschtein TA, Peeters M, Shalom D, and Sigman M (2011). Sea slugs, subliminal pictures, and vegetative state patients: boundaries of consciousness in classical conditioning. Frontiers in psychology, 2 PMID: 22164148

Young, Canadian and on Antipsychotics

Antipsychotic use in Canadian children and teens is rising dramatically - prescriptions more than doubled in just 4 years, from 2005 to 2009.

That's according to a paper just out from Pringsheim et al. It's been known for a while that broadly the same is true of the USA. The data reveal that the Canadian border is no barrier to the spread of antipsychotics.

What's surprising is that while in the USA, some of these drugs are officially licensed for use in certain children and adolescent psychiatric disorders, in Canada all such use is off-label. That didn't stop there being nearly 700,000 youth prescriptions for an antipsychotic in 2009, in a country with a total population of 35 million - although bear in mind that this includes multiple prescriptions for the same person.

The growth in antipsychotics is accounted for by the second-generation "atypical" antipsychotics. Risperidone (Risperdal) was the biggest success story accounting for well over half of the total.


What's disturbing about this, as I've said before, is not so much the fact that these drugs are being used but the speed of the growth. It represents a fundamental shift in the way children and adolescent mental health problems are treated, one which has happened so fast that it's hard to believe that there was time to properly think through the consequences...

Use of SSRI antidepressants and psychostimulants (mainly ADHD drug methylphenidate, Ritalin) also rose between 05 and 09, but only by about 40%. That means that there were more antipsychotic than SSRI prescriptions in children and teens by 09, which is pretty remarkable.

Only 13% of the youth antipsychotic recommendations were actually for psychosis, the original indication of the drugs. The leading diagnosis was ADHD, which is odd, because the main drugs for ADHD, such as Ritalin, boost dopamine release, while antipsychotics block dopamine's effects via D2 receptors.


Other popular indications were mood disorders and conduct disorders. Overall, the fact that the vast majority of the antipsychotic prescriptions were not for psychosis confirms the view that the term "antipsychotic" for these drugs is misleading.

Pringsheim T, Lam D, and Patten SB (2011). The Pharmacoepidemiology of Antipsychotic Medications for Canadian Children and Adolescents: 2005-2009. Journal of child and adolescent psychopharmacology PMID: 22136092

"Mad Honey" Sex Is A Bad Idea

A cautionary tale from Turkey - do not eat poison honey to try to spice up your sex life.

"Mad honey" is honey made by bees from the nectar of toxic Rhododendron flowers. In places where wild Rhododendrons grow, including Turkey, it's a health hazard. The dangers of mad honey were known to the ancient Greeks and Romans, and it's reported that leaving tainted honeycombs in the path of invading armies was a popular military tactic.

2000 years later, some people still haven't quite got the message. According to a case report from cardiologists Yarlioglues et al, a married couple deliberately ate some mad honey "for reasons of sexual performance".

After eating one teaspoon per day for a week, they decided to crank it up a notch and ate a full tablespoon of the stuff. But their attempt to heighten their Turkish delight quickly turned sour, as they both suffered symptoms of confusion, chest pain, low blood pressure and slowed heartbeat. After presenting themselves to hospital, doctors discovered that they had both suffered an acute inferior myocardial infarction - a mild heart attack.

It's not clear whether the sex was a contributing factor.

The randy Rhododendron fans were lucky - following treatment, they both recovered. In fact, the authors say "To our knowledge, no fatal cases of mad-honey poisoning have been reported since ancient Roman times." However, it seems that some people are still willing to try their luck.

The toxin in mad honey is gryanotoxin. It acts by potentiating the opening of sodium channels, which are found both in the heart and the brain. This may be why it produces a combination of cardiovascular and psychoactive effects.

Mikail Yarlioglues et al (2011). Mad-Honey Sexual Activity and Acute Inferior Myocardial Infarctions in a Married Couple Texas Heart Institute Journal

Genes for Intelligence - Back to Square One

Here's a paper - soon to appear in Psychological Science - which says that Most Reported Genetic Associations with General Intelligence Are Probably False Positives

The authors tried to replicate published associations between particular genetic variants (SNPs) and IQ (specifically the g factor). They looked at three datasets, a total of about 10,000 people, and didn't confirm any of the 12 associations.

As Razib Khan says in his post on this, "My hunch is that these results will be unsatisfying to many people." I'd go further and say that no-one will be happy with these.

For those who believe that IQ is purely environmental and not genetic, any satisfaction they might feel will be short lived because these authors did replicate the recent finding that genetic variants explain about 50% of the variance in IQ. Looking at all SNPs together, there was a strong correlation between "genetic similarity" and similarity in IQ. That independently confirms what the much-criticized twin studies of IQ said - IQ is about 50% heritable.

But for people who do believe in the genetics of intelligence, this shows us that we have no idea what the genes are, and that everything published so far has been pretty much for naught.

There's another implication. We actually do know of many "IQ genes" in that we know genes that, when mutated, cause mental retardation (very low IQ).

Now many researchers have hoped that if a certain gene causes you to have an IQ of, say, 50 when it's completely deleted by a mutation, then more subtle variants in that gene would have minor effects on IQ. Maybe a variant that reduces expression of the gene by 10% would knock off 5 IQ points.

In other words, if big mutations cause big phenotypes, then small mutations in the same place ought to cause small phenotypes. It seems to make sense - but today's IQ literature shows that it's just not true.

That's not just a problem for IQ though. Take autism or ADHD, we know that there are rare, severe mutations that cause these conditions. Many people are hoping that common variation in the same genes might also be interesting - but if IQ is anything to go by, it won't be.

Perhaps this is not so surprising. Breaking your neck and becoming paraplegic is going to seriously impair your ability to play baseball. That doesn't mean that normal variation in baseballing skill has much to do with minor neck injuries.

Chabris, C. F. et al (2011). Most Reported Genetic Associations with General Intelligence Are Probably False Positives Psychological Science

Do Antidepressants Make Some People Worse?

Antidepressants may help depression in some people but make it worse for others, according to a new paper.

This is a tough one so bear with me.

Gueorguieva, Mallinckrodt and Krystal re-analysed the data from a number of trials of duloxetine (Cymbalta) vs placebo. Most of the trials also had another antidepressant (an SSRI) as well. And the SSRIs and duloxetine seemed to be indistinguishable so from now on I'll just call it antidepressants vs. placebo as the authors did.

People on placebo got, on average, moderately better over 8 weeks.

People on antidepressants fell into two classes. The largest class got, on average, a lot better. But about 25% did poorly, staying just as depressed as before. This "nonresponder" group did much worse than the placebo group - again on average. Here you can see the mean "trajectories" of depression symptoms (HAMD scores) in the three groups:

This raises the scary possibility that while antidepressants are helping some people, they're harming others. But hang on. It's complicated.

First off, maybe this is all a statistical illusion. When the authors say that the people on drug fell into two classes, what they mean is that when you try to model the data according to a certain mathematical model, assuming either 1, 2, 3 or 4 underlying classes, the 2 class solution was the best fit. While for placebo a 1 class solution was best.

We considered linear, quadratic, and cubic trends over time, with between 1 and 4 trajectory classes. We also considered piecewise models with a change point at 2 weeks, linear change before week 2, and quadratic change after week 2. The selection of the best model was based on the Schwartz-Bayesian information criterion and on the Lo-Mendell-Rubin (LMR) likelihood ratio test...

That's nice... but they don't present the raw data. They don't tell us whether, looking at the individual trajectories of people on antidepressants, you'd actually see two classes. What I want is a graph of how likely people are to get better by a certain amount. If Gueorguieva et al are right, I want it to look like this i.e. bimodal -

We're not shown this graph. I'll eat my hat if it does look like that, frankly, because if it did people would have noticed the bimodality in antidepressant trials ages ago.

True, statistical models can tell us things that aren't obvious by inspection, so even if this isn't what the data look like, they might still be right. It could be that the two "peaks" are so broad, and there's so much random noise, that they blur into one.

However, it's also true that you can fit an infinite number of models to any set of data and at some point you have to step back and say - am I making this more complicated than it needs to be?

It could be that a 2-class model is better than a 1-class model for the people on antidepressants, but only because they're both crap, and really, every patient has a different, unpredictable trajectory which is poorly captured by such models.

Let's assume however that this is true. What would it mean?

Firstly, the fact that one class of people on antidepressants does worse than people on placebo doesn't mean that antidepressants are harming them. The authors miss this point, when they say

there are 2 trajectories for patients treated with antidepressants and 1 trajectory for patients treated with placebo [so] some patients would seem to be more effectively treated with placebo than with a serotonergic antidepressant.

But that's fallacious. It treats a purely statistical entity as representing individual people. Suppose that what antidepressants do is to take people who, on placebo, would have improved a bit, and make them improve a bit more than they otherwise would have. You'd then end up with more people doing well, but also fewer people doing moderately because they'd have been "moved up" out of the middle ground.

That "nudging people off the fence" could lead to a bimodal distribution and two distinct classes. But in this case the people doing badly would have done badly either way. The drug didn't make them do badly, it just made doing-badly into a class. On the other hand it's consistent with antidepressants doing real harm. We can't tell.

We do know that other randomized controlled trials show very convincingly that in a small minority of people, mostly but not exclusively young people, antidepressants do worsen suicidal thoughts and behaviours. So it's plausible. But we just don't know yet.

What worries me is that this paper is the latest in a series of attempts  to use, well, creative statistical approaches to antidepressant trial data. This one is nowhere near as dodgy as the Cherrypicker's Manifesto I discussed last year, but it cites that paper and others by the same group. The first sentence of the Abstract of this paper makes the intention clear:

The high percentage of failed clinical trials in depression may be due to high placebo response rates and the failure of standard statistical approaches to capture heterogeneity in treatment response.

In other words, the reason clinical trials of new antidepressants often fail to show a benefit over placebo is not because the drugs are crap but because the statistics aren't subtle enough. And you can see where this is going: if only we could use statistical models to find the people who do benefit from antidepressants, and compare them to placebo, there'd be no problem...

Gueorguieva R, Mallinckrodt C, and Krystal JH (2011). Trajectories of depression severity in clinical trials of duloxetine: insights into antidepressant and placebo responses. Archives of General Psychiatry, 68 (12), 1227-37 PMID: 22147842

The Brain's High School Spot

It's been known for a long time that electrical stimulation of the brain's temporal lobe can sometimes evoke vivid memories.

The famous neurosurgeon Wilder Penfield first noticed this effect as part of his pioneering stimulation experiments, but he believed that it was both uncommon and haphazard with any given stimulation able to evoke any memory, more or less at random.

A new paper, however, says different. Philadelphia's Joshua Jacobs et al report that they found a spot in the left temporal lobe of a male patient, stimulation of which evoked memories of the man's time at high school. The guy was in his 30s at the time, so these are quite distant memories.

When it first happened, he is reported to have said:

Iʼm, like, remembering stuff from, like, high school…. Why is this suddenly popping in my head?

Repeated stimulation of the same electrode - but not nearby electrodes - caused other high school memories to emerge.

Even more interestingly, when the same stimulating electrode was used to record activity during memory retrieval, the "high school spot" was found to be significantly less active when high school was being remembered, compared to when various other kinds of memories were being accessed.

This graph shows that all kinds of memories evoked high-frequency activity in the high-school zone, but high-school memories did so less:

No other electrode location caused the same effects (or indeed, any detectable memory effects), although as you can see on the image at the top, the electrode coverage was not huge.

A little background: the guy had these electrodes in place because he suffered from epilepsy, resistant to medication, which was believed to originate in the temporal lobe. Temporal lobe epilepsy can cause memory phenomena rather like this, but this patient had never experienced that, and the electrically-evoked memories were experienced as entirely novel.

It's a nice case report and it raises many questions. Why is the high-school spot less active during memory retrieval? That seems the wrong way around (I did a double-take to make sure I was reading it properly).

And what would happen if you somehow disabled (or overactivated) this area, and asked him to remember a particular school memory? Would he draw a blank, or would he remember it but without the "high-school-ness"? What would that feel like?

Either way, this case suggests that memories are stored in the brain "by topic", in the sense that "similar" memories are associated with nearby areas of the brain. At least sometimes. But then, why didn't nearby electrodes evoke other memories? If there's a high-school spot, why not a kindergarten spot, a my-first-job spot?

Maybe those spots lay in areas with no electrode coverage... but the fact that many temporal electrodes didn't bring back any memories suggests that there's lots of cortex which isn't part of a "spot". Perhaps those areas are "spare", waiting to be used up? Clearly, he wasn't born with a high school spot. It must have emerged during high school. But in that case there had to be a "blank" area first.


Jacobs J, Lega B, and Anderson C (2011). Explaining How Brain Stimulation Can Evoke Memories. Journal of cognitive neuroscience PMID: 22098266

Scientific Databases - or Filters?

A new online database called AutismKB offers a quick way to find the evidence linking genes to autism.

You can read up on it in a paper describing the project.

You can browse by chromosome or gene name, it includes data on all kinds of genetic variants from SNPs to CNVs and it gives each variant a score according to the strength of the evidence. I haven't had a chance to really tell how useful these scores are, but there's an option to create your own score based on how much weight you give different kinds of evidence. The dataset is huge although it doesn't seem to have been updated for a few months.

Overall, it's a new tool and there's sure to be bugs to iron out, but it seems like it could be very useful. I do worry though that this kind of database encourages misleading ways of thinking about autism genetics.

There are numerous genetic variants which have been strongly linked to autism, although none of them account for more a small proportion of cases because these variants are rare. But many (most, actually, is my impression) of them have also been observed in people with other symptoms ranging from ADHD to epilepsy to schizophrenia.

So searching a database of "autism genes" could encourage you to think that these were only autism genes, which is far from true. Genetics, it is becoming increasingly clear, doesn't respect our current concepts of psychiatric illness or our academic specialities. There are few (if any) parts of the genome that can be neatly fenced off and declared exclusive to ADHD experts, schizophrenia researchers or whatever.

But disease-specific databases encourage the illusion that they do exist. It's the same old problem of the filter bubble which many people have warned about in the context of general purpose search engines. Scientists have filter bubbles too.

This is not of course a criticism of AutismKB in particular - the same goes for any similar "disease-gene" database. And to be fair AutismKB does provide links to a schizophrenia database, and a couple of others but you have to dig quite deep to get there. The "main page" of results for any given variant is pure autism.

That's the whole problem with filter bubbles - they make it too easy to hear what you want to hear, compared to getting a new perspective, so you don't even think to look outside the filter.


Xu LM, Li JR, Huang Y, Zhao M, Tang X, and Wei L (2011). AutismKB: an evidence-based knowledgebase of autism genetics. Nucleic acids research PMID: 22139918

The Network of Mental Illness

A provocative but problematic paper just out offers a new perspective on psychiatric symptoms.

The basic idea is that rather than psychiatric disorders being entities, they are just bundles of symptoms which cause each other:

...symptoms are unlikely to be merely passive psychometric indicators of latent conditions; rather, they indicate properties with autonomous causal relevance. That is, when symptoms arise, they can cause other symptoms on their own. For instance, among the symptoms of MDE we find sleep deprivation and concentration problems, while GAD (generalized anxiety disorder) comprises irritability and fatigue. It is feasible that comorbidity between MDE and GAD arises from causal chains of directly related symptoms; e.g., sleep deprivation (MDE)→fatigue (MDE)→concentration problems (GAD)→irritability (GAD).

The authors seem to have mixed up their labels in the middle there, but you see the drift.

This symptom-based approach stands in contrast to the idea that psychiatric illnesses are underlying things which lead to some symptoms. So it's a challenge to the notion of underlying biological dysfunction (except maybe for specific symptoms) but it's equally incompatible with any theory of underlying psychological causes - there's no room for Freudian unconscious "complexes" here.

So there's something very straightforward and un-mysterious about this model, which will either make it attractive or suspect, depending on whether you think human life is mysterious or not.

What's the evidence? First, the authors do an analysis of the DSM-IV diagnostic manual in terms of symptoms. They take every symptom which is mentioned in at least one diagnosis. They found 439 symptoms in total, over 201 disorders, with many symptoms, such as insomnia, shared between lots of different "disorders".

They then used network analysis to create a kind of graph where the "distance" between the nodes (symptoms) is based on the number of shared diagnoses. They found that while some symptoms are unique to just one disorder, there's a core of highly shared symptoms which form a "giant component"

It's a very clever approach but I wonder what it really tells us. The DSM-IV is not data about mental illness. It's data about what we think about mental illness. Actually, it's not even that: it's data about what a particular set of people, at a particular time, were able to agree upon.

DSM-V is coming soon, and before that we had DSM's I, II and III. What about them? Do they have a different network structure? I'd have thought they would, but we don't know.

We've already seen the kinds of politics that lie behind the decision to include or exclude a diagnosis in the DSM. In the upcoming DSM-V they're seriously proposing to add a new diagnosis ("TDDD"), purely in order to stop people getting another diagnosis (childhood "bipolar").

There is a lot of symptom overlap between TDDD and bipolar disorder. Because one was designed for the purpose of diverting patients from the other. But that doesn't tell us anything about real people with real symptoms. This is an extreme example and to be fair to the authors they do acknowledge some of these problems with the DSM, but still.

The authors then show that the symptomatic closeness between DSM-IV disorders predicts the rates of comorbidity between those disorders, as measured in the American population survey the NCS-R. This is true even of disorders which don't share a common symptom but which are connected indirectly by a mutual friendship, as it were.

Finally they show that a statistical model based on interacting symptoms can predict the prevalence of depression (10% per year according to the NCS-R survey) and GAD (3% per year). It does so much better than a random model in which symptoms randomly interact.

However, I'm not convinced that all these show us that the symptom-network approach is the best model to explain the occurence of these disorders. It only shows us that it's a model that works better than a crazy random model. I'm also not sure that being able to model the NCS-R data is even a good thing, since these data are themselves of questionable validity.

But it's a genuinely interesting approach and well worth following up.

Borsboom D, Cramer AO, Schmittmann VD, Epskamp S, and Waldorp LJ (2011). The small world of psychopathology. PloS one, 6 (11) PMID: 22114671

A Psychedelic Tale of Two Neurotransmitters

An unexpected interaction between neurotransmitter systems may explain psychosis and hallucinations, according to a fascinating new paper.

Serotonin (5HT) and glutamate are two neurotransmitters. Up until now, it was thought that they acted independently. A given neuron might have receptors for both serotonin and glutamate, but they didn't interact: serotonin would never affect the glutamate receptors, and vice versa.

The new research overturns that view. Authors Miguel Fribourg and colleagues of Mount Sinai School of Medicine show, in a series of elegant experiments in mice, that different receptors can cluster together, forming a complex. The two receptors, serotonin's 5HT2A and glutamate's mGluR2, can talk to each other.

However, this doesn't seem to happen under normal conditions. Serotonin and glutamate don't seem to trigger the receptor interaction, or at least not very much. Only certain drugs can do it. And this is where it gets really interesting.

Psychedelic drugs, like LSD, have long been thought of as 5HT2A agonists, binding to the receptor and activating it. It turns out that this was only half right. They also inhibit mGluR2 transmission via the receptor complex. Serotonin itself is a 5HT2A agonist, but it doesn't do that. So psychedelics seem to be a kind of (for want of a better word) "superagonist".

It also works in reverse. The antipsychotic drugs clozapine and risperidone are known as 5HT2A antagonists. But Fribourg et al show that they also activate the mGluR2 receptor.

And the cross-talk can go in the other direction. Certain molecules that act on mGluR2 can either inhibit or promote 5HT2A. Unlike psychedelics and antipsychotics, these mGluR2 drugs have not been tested in humans yet. But these data predict that they will have psychedelic-like or antipsychotic-like effects, depending which way they work.

The interaction turns out to be all about G proteins, which are part of the chain of transmitter substances that convey signals within the cell, in response to neurotransmitters outside it. Here's a chart showing the effects of various drugs on the balance between different G proteins: the LSD-like psychedelic DOI has the opposite effect from the antipsychotics clozapine and risperidone.

This paper builds on a previous one from the same team showing that psychedelic 5HT2A "agonists" (like LSD and DOI) have different effects on G proteins from other, non-psychedelic agonists. That was interesting in itself but by adding glutamate to the picture, this new paper is really ground-breaking.

This goes a long way to explaining one of the mysteries of serotonin which is this:  if 5HT2A agonists like LSD are psychedelic, why aren't antidepressants the same? Almost all antidepressants work by increasing extracellular 5HT levels. That ought to mean that they activate 5HT2A receptors (indirectly). This explains why not - 5HT alone doesn't promote the crucial 5HT2A-mGluR2 interaction.

Taken together, these interesting results show clearly that 5HT2A and mGluR2 are hooking up and doing something exciting. Certainly in terms of how hallucinogens work.

I'm less convinced that this can directly explain antipsychotic effects though. The problem is that while newer "atypical" antipsychotics act on 5HT2A, the older antipsychotics don't, and atypicals are at best only slightly more effective on average.

What we don't yet know is whether this kind of complex receptor interactions can happen with other receptors. I'd have thought it unlikely that these two receptors were the only ones that could ever do it. The synapse looks like it's more complex than we could have imagined.

Fribourg M, et al. (2011). Decoding the Signaling of a GPCR Heteromeric Complex Reveals a Unifying Mechanism of Action of Antipsychotic Drugs. Cell, 147 (5), 1011-23 PMID: 22118459

Beware Good Theories

The ancient Greeks had a lovely theory. Certain places on the earth (caves, mostly) were, they thought, gateways to the underworld. Plants growing near these places could absorb the deadly essence of Hades and became poisonous.

Snakes and other venemous creatures got their poison by consuming these plants. And stinging insects got their little doses of poison by feeding off dead snakes.

Isn't that a great narrative? It explains everything, in a nice logical progression. OK, it presupposes what we would call a "supernatural" force as the ultimate origin of poison, but other than that, it's an entirely "scientific" account. In accordance with Occam's Razor, it proposes a single unified process underlying diverse phenomena.

It is, in other words, a perfect scientific theory. It's completely wrong, on every point, but we only know that because we now understand atoms, molecules, chemistry and biochemistry, which the Greeks had no way of knowing. At the time, the Hades theory was surely the best possible theory about where poison came from.

The moral of this story is, beware nice theories based on incomplete data.


Reference: Greek Fire, Poison Arrows and Scorpion Bombs, which I'm currently reading, all about chemical and biological weapons.