Royal College Press Office: Do they read or understand their own papers?

There's a retrospective study in this month's issue of The Psychiatrist titled: "Use of anti-dementia drugs and delayed care home placement: an observational study". It's not the best study in the world but the authors appropriately acknowledge the limitations, explicitly stating in the abstract that: "However, based on purely observational data, no conclusion can be made as to whether such association is causal."

It was a retrospective study which means that it couldn't compensate for all sorts of factors that may have confounded the finding that, "...there was a delay in care home placement by a median of 12 months in those who took ChEIs compared with those who did not." This is not the first study to suggest that anti-dementia drugs may delay admission to care homes, and many other studies were much better designed and prospective. Importantly, the authors state: "...at the end of the follow-up there was no significant reduction in the probability of being in a care home setting between those who had taken ChEIs compared with those who had not." So, the drugs didn't prevent care home admission, only that those that took drugs were admitted to care homes later than those that didn't. The authors mention that the groups weren't matched and only suggest that there weren't differences. However, no comparisons are reported and the authors don't provide detail on the factors that they themselves report as potential confounders.

It's not possible to know, for example, if those that took anti-dementia drugs were of a less-advanced stage or if they had less comorbidity - neither of these things appear to have been corrected for. This means that more unwell patients might have been considered unsuitable for the drugs and their course of illness would mean that they were already closer to admission. Since the two groups (receiving drug and control) weren't described in detail (in terms of age, diagnosis, severity of illness, medical illness) we can't be sure if the drugs had anything to do with it.

You might hope that such limitations would be taken into account. But the RCPsych press office announce that:

Anti-dementia drugs may help delay people’s admission to care homes

This is precisely what the study didn't say and what the authors were careful to caution against concluding. Still, it seems that the scientific credibility of the RCPsych is less important than getting 'good news' headlines.

New Paper on STAR*D - Is all as it seems?

A recent paper commenting on the outcomes from the STAR*D Study (Full paper for download: Pigott, H. E., Leventhal, A. M., Alter, G. S., et al (2010) Efficacy and Effectiveness of Antidepressants: Current Status of Research. Psychotherapy and Psychosomatics, 79(5): 267-279 revisits some of the ground covered by Irving Kirsch but interestingly looks again at the outcomes from STAR*D.

Most people will recall that STAR*D was a large (over 4,000 patients enrolled) and expensive (about $35 million) trial which attempted to determine what the 'real world' outcomes were for four steps of antidepressant therapy (drugs and psychological therapy). It covered a range of different comparisons, and perhaps the 'quickest' overview of what was a complex trial can be found in this paper: Rush, A. J., Trivedi, M. H., Wisniewski, S. R., et al (2006)American Journal of Psychiatry, 163(11): 1905-1917 Acute and Longer-Term Outcomes in Depressed Outpatients Requiring One or Several Treatment Steps: A STAR*D Report. [Link to Journal Website]

A summary of the steps (and to some extent, outcomes) is shown below:

STAR*D used the Quick Inventory of Depressive Symptomatology (16-items) as one of their main outcome measures, and outcomes from each treatment step, using the QIDS-16 were as follows:

• Step 1 = 36.8%
• Step 2 = 30.6%
• Step 3 = 13.7%,
• Step 4 = 13.0% 

The overall [cumulative] remission rate was 67%. This means that overall, two thirds of patients achieved remission. It also means that after four treatment trials, one third had not remitted.

It's important to note that this cumulative remission rate was "hypothetical" in that it assumed no drop-outs. Of course, every trial has drop-outs, and this is what Pigott et al have taken into account. They also make some other criticisms of STAR*D:

1. The use of the QIDS-16 as a primary outcome measure instead of the 30-item scale. The main reason for this was apparently the large number of missing measurements on the latter. However, the QIDS-16 is critiqued by Pigott et al as being used as a 'clinical' measure rather than a 'research' measure throughout the study, and that its use as a study outcome might be unjustified.
2. They also comment on the cut-offs that were used on the Hamilton Rating Scale for Depression (HRSD, or HAM-D). Pigott et al report that 931 patients who should have been excluded because their HRSD score was ≤ 14 (an exclusion criterion for the study, which excludes those with very mild depression - i.e. non-major depression). They argue that this "inflated" the original remission rate for Step 1 from 32.8% to 36.8%.

They go on to present slightly modified remission rates for each step, along with the drop-out rates for each step:

Pigott et al conclude by discussing the fact that remission from major depression is hard to achieve. Perhaps this is not surprising to those who treat depression. Of course, we know that antidepressants aren't as effective for those with milder forms of the illness but antidepressants are probably one of the treatments for depression with the greatest evidence base. STAR*D also included Cognitive Behavioural Therapy (CBT) which is probably the best-evidenced psychological treatment for this population.

Should it really be a surprise that antidepressants don't work for everyone? Hopefully not. However, it is not clear what the authors might be suggesting as an alternative until you get to the 'Conflicts of Interest' section:

H. Edmund Pigott, PhD, and Gregory S. Alter, PhD, are founders of NeuroAdvantage, LLC, a for-profit neurotherapy company. During the past 3 years, Dr. Pigott has consulted for CNS Response, Midwest Center for Stress and Anxiety, and SmartBrain Technologies.

That's right, the authors own their own company, Neuroadvantage, which will sell you (for $995), a device that plays sounds and lights in order to synchronise your brain waves. They claim that it "Helps to Decrease Symptoms of Depression & Anxiety". No wonder that they were keen to weaken the case for drugs and psychological therapies - they have a product which they wish to sell that is targeted at the same market.

As with all such products, "This patented technology is based on over 70 years of research and takes advantage of our mind’s natural tendency to synchronize with pleasant rhythmic stimulation". Not only is the 'technology' old (and therefore established), it links in to natural tendencies.

So keen are the authors/ salesmen to ensure that you consider their product, they provide a link to the paper above (it is free to download) to viewers of the website. This is, arguably, a classic case of 'bait and switch'. There is a very good article on 'bait and switch' available here, but essentially the bait is a treatment that avoids the side effects and apparent ineffectiveness of drugs and therapy, and once lured in, the switch is to unproven therapies with much less evidence.

How much less will be the subject of a subsequent post.

BBC website reports that, "'Green' exercise quickly 'boosts mental health'"

The BBC (and other sites) are reporting a study that apparently claims that "'Green' exercise quickly 'boosts mental health'". The study has been picked up by the US National post, and the UK Daily Mail.

The authors were Jo Barton and Jules Pretty (personal page at University of Essex here) and the study was published in the Environmental Science and Technology journal.

There are some bold claims, such as:

1. "The biggest effect was seen within just five minutes."
2. "A bigger effect was seen with exercise in an area that also contained water - such as a lake or river."

The paper can be found here (Abstract only | subscription required for full paper).

The authors state: "The research used meta-analysis methodology to analyze 10 UK studies involving 1252 participants." It doesn't say that it was a meta-analysis, only that it used the methodology (sic) of meta-analysis. Of course, you can only really meta-analyse studies with a degree of homogeneity and the conclusions one can draw from such reviews depend greatly on the quality of the underlying studies. Poorly-controlled and heterogenous studies with wild estimates of effect sizes don't lend themselves to robust systematic review.

Another alarm bell starts ringing when one reads, "Outcomes were identified through a priori subgroup analyses". Okay, the sub-groups were determined a priori, but subgroup analysis is often used as a way of mining the data for some significant finding. The BMJ has a recent article on the credibility of subgroup analyses.


It's surprising that the study also reported, "Dose responses for both intensity and duration showed large benefits from short engagements in green exercise, and then diminishing but still positive returns." This is counter-intuitive. If exercise is so good, why does it get less effective the more you do of it? I doubt the included studies were looking at elite athletes who may have been overtraining - the authors are reporting that more exercise is less beneficial for most of the reported outcomes (e.g. self-esteem).

It's clear that Jules Pretty is favourably disposed to exercise in green environments (who wouldn't be?), but previous 'reviews' would indicate that reported benefits in different studies are taken at face value, and not critically appraised in the way that they should be. For example, many studies in exercise for depression look at those with mild depressive illness which is, for many people, a self-limiting condition. The fact that someone feels better after a six-week course of exercise may have little to do with the exercise per se, and more to do with the natural course of the illness.

The 2009 Cochrane Review of Exercise for Depression concluded: "Exercise seems to improve depressive symptoms in people with a diagnosis of depression, but when only methodologically robust trials are included, the effect sizes are only moderate and not statistically significant." Essentially, when you exclude poorly-conducted trials, the effects of exercise are not statistically different from those that you would see with chance alone.

Lidocaine brain injections for anxiety...not.

Just under a fortnight ago, the Daily Mail printed an article entitled: "The injection that can cure phobias... unless, of course, you're terrified of needles". In it, the reporter (David Derbyshire, listed as the Environmental Correspondent) suggested that the research, "...could lead to new treatments for phobia." Indeed, the comments section (no longer available on the Daily Mail website) included people who were suggesting that they would sign up for injections to cure their phobias.

The article was reporting a study by Japanese researchers (open access):

Yoshida M, Hirano R. Effects of local anesthesia of the cerebellum on classical fear conditioning in goldfish. Behavioral and Brain Functions. 2010;6(1):20. (Paper here)

The study appeared to be either a replication of a similar study by the same lead author, which involved a number of methods (cooling, ablation) to 'inactivate' the goldfish cerebellum.

Yoshida M, Okamura I, Uematsu K. Involvement of the cerebellum in classical fear conditioning in goldfish. Behavioural Brain Research. 2004;153(1):143-148. (Paper here | Not open access)

In the study, they essentially used an electric shock as the unconditioned stimulus, and light as the conditioned stimulus. In response to the shock, goldfish will naturally exhibit slowing of the heartbeat (bradycardia), and by repeated pairings of the light and the shock, they were able to cause the goldfish to demonstrate bradycardia in response to the light alone. The basic process of classical conditioning is explained at Wikipedia.

Injecting lidocaine into the cerebellum had no effect on the goldfishes response to the first light stimulus nor the electric shock. However, it was found that goldfish with lidocaine in their cerebellums were less able to learn the association between the light and the shock.


So, a superficial glance might suggest that anaesthetising your cerebellum might stop you from getting anxious.

There are some problems with the interpretation of this study demonstrated by the press that picked it up:

1. For many people, a simple phobia might not be so problematic as to warrant injections of local anaesthetic into their cerebellums. Since the cerebellum is essential (in humans) for the coordination and sequencing of complex motor actions, anaesthetising it might result in you being unable to move out of the way of one's feared stimulus. But of course, you will no longer be afraid of it.
2. Classical fear conditioning is not the only learning mechanism involved in the maintenance of phobic responses. In more complex organisims (such as humans), instrumental learning/ operant conditioning also plays a part, and not all phobias have a classical conditioning explanation.
3. There are already effective treatments for most anxiety disorders, and simple phobias. Graded exposure has been around for decades, but due to the emphasis of mental health services on 'severe' mental disorders, many of these simple behavioural treatments have been left out of many people's therapeutic armamentarium.
4. Such a 'treatment' would only prevent the acquisition of a specific association, and there is nothing to suggest that you can wipe out a fear of spiders with an injection that would, of course, be temporary.

I would be surprised if we were seeing lidocaine injections into the brain being available on the NHS at anytime in the near future.