How our current reward structures have distorted and damaged science

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Two things almost everyone would agree with:

1. Good scientists do research and publish their results, which then have impact on other scientists and the broader community.

2. Science is a competitive business: there is not enough research funding for everyone, not enough academic jobs in science, and not enough space in scientific journals. We therefore need ways of ensuring that the limited resources go to the best people.

When I started in research in the 1970s, research evaluation focused on individuals. If you wrote a grant proposal, applied for a job, or submitted a paper to a journal, evaluation depended on peer review, a process that is known to be flawed and subject to whim and bias, but is nevertheless regarded by many as the best option we have.

What has changed in my lifetime is the increasing emphasis on evaluating institutions rather than individuals. The 1980s saw the introduction of the Research Assessment Exercise, used to evaluate Universities in terms of their research excellence in order to have a more objective and rational basis for allocating central funds (quality weighted research funding or QR) by the national funding council (HEFCE in England). The methods for evaluating institutions evolved over the next 20 years, and are still a matter of debate, but they have subtly influenced the whole process of evaluation of individual academics, because of the need to use standard metrics.

This is inevitable, because the panel evaluating a subject area can't be expected to read all the research produced by staff at an institution, but they would be criticised for operating an 'old boy network', or favouring their own speciality, if they relied just on personal knowledge of who is doing good work – which was what tended to happen before the RAE. Therefore they are forced into using metrics. The two obvious things that can be counted are research income and number of publications. But number of publications was early on recognised as problematic, as it would mean that someone with three parochial reports in a journal of national society would look better than someone with a major breakthrough published in a top journal. There has therefore been an attempt to move from quantity to quality, by taking into account the impact factor of the journals that papers are published in.

Evaluation systems always change the behaviour of those being evaluated, as people attempt to maximise rewards. Recognising that institutional income depends on getting a good RAE score, vice-chancellors and department heads in many institutions now set overt quotas for their staff in terms of expected grant income and number of publications in high impact journals. The jobs market is also affected, as it becomes clear that employability depends on how good one looks on the RAE metrics.

The problem with all of this is that it means that the tail starts to wag the dog. Consider first how the process of grant funding has changed. The motivation to get a grant ought to be that one has an interesting idea and needs money to investigate it. Instead, it has turned into a way of funding the home institution and enhancing employability. Furthermore, the bigger the grant, the more the kudos, and so the pressure is on to do large-scale expensive studies. If individuals were assessed, not in terms of grant income, but in terms of research output relative to grant income, many would change status radically, as cheap, efficient research projects would rise up the scale. In psychology, there has been a trend to bolt on expensive but often unmotivated brain imaging to psychological studies, ensuring that the cost of each experiment is multiplied at least 10-fold. Junior staff are under pressure to obtain a minimum level of research funding, and consequently spend a great deal of time writing grant proposals, and the funding agencies are overwhelmed with applications. In my experience, applications that are written because someone tells you to write one are typically of poor quality, and just waste the time of both applicants and reviewers. The scientist who is successful in meeting their quota is likely to be managing several grants. This may be a good thing if they are really talented, or have superb staff, but in my experience research is done best if the principal investigator puts serious thought and time into the day-to-day running of the project, and that becomes impossible with multiple grants.

Regarding publications, I am old enough to have been publishing before the RAE, and I'm in the fortunate but unusual position of having had full-time research funding for my whole career. In the current system I am relatively safe, and I look good on an RAE return. But most people aren't so fortunate: they are trying to juggle doing research with teaching and administration, raising children and other distractions, yet feel under intense pressure to publish. The worry about the current system is that it will encourage people to cut corners, to favour research that is quick and easy. Sometimes, one is lucky, and a simple study leads to an interesting result that can be published quickly. But the best work typically requires a large investment of time and thought. The studies I am proudest of are ones which have taken years rather than months to complete: in some cases, the time is just on data collection, but in others, the time has involved reading, thinking, and working out ways of analysing and interpreting data. But this kind of paper is getting increasingly rare. As a reviewer, I frequently see piecemeal publication, so if you suggest that a further analysis would strengthen the paper, you are told that it has been done, but is the subject of another paper. Scholarship and contact with prior literature has become extremely rare: prior research is cited without reading it – or not cited at all – and the notion of research building on prior work has been eroded to the point that I sometimes think we are all so busy writing papers that we have no time to read them. There are growing complaints about an 'avalanche' of low-quality publications.

As noted above, in response to this, there has been a move to focus on quality rather than quantity of publications, with researchers being told that their work will only count if it is published in a high-impact journal. Some departments will produce lists of acceptable journals and will discourage staff from publishing elsewhere. In effect, impact factor is being used as a proxy for likelihood that a paper will be cited in future, and I'm sure that is generally true. But just because a paper in a high impact journal is likely to be highly cited, it does not mean that all highly-cited papers appear in high impact journals. In general, my own most highly-cited papers appeared in middle-ranking journals in my field. Moreover, the highest impact journals have several limitations:

1. They only take very short papers. Yes, it is usually possible to put extra information in 'supplementary material', but what you can't do is to take up space putting the work in context or discussing alternative interpretations. When I started in the field, it was not uncommon to publish a short paper in Nature, followed up with a more detailed account in another, lowlier, journal. But that no longer happens .We only get the brief account.

2. Demand for page space outstrips supply. To handle a flood of submissions, these journals operate a triage system, where the editor determines whether the paper should go out for review. This can have the benefit that rejection is rapid, but it puts a lot of power in the hands of editors, who are unlikely to be specialists in the subject area of the paper, and in some cases will explicit in their preference for papers with a 'wow' factor. It also means that one gets no useful feedback from reviewers: viz my recent experience with the New England Journal of Medicine, where I submitted a paper that I thought had all the features they'd find attractive – originality, clinical relevance and a link between genes and behaviour. It was bounced without review, and I emailed, not to appeal, but just to ask if I could have a bit more information about the criteria on which they based their rejection. I was told that they could not give me any feedback as they had not sent it out for review.

3. If the paper does go out for review, the subsequent review process can be very slow. There's an account of the trials and tribulations of dealing with Nature and Science which makes for depressing reading. Slow reviewing is clearly not a problem restricted to high impact journals. My experience is that lower-impact journals can be even worse. But the impression from the comments on FemaleScienceProfessor's blog, is that reviewers can be unduly picky when the stakes are high.

So what can be done? I'd like to see us return to a time when the purpose of publishing was to communicate, and the purpose of research funding was to enable a scientist to pursue interesting ideas. The current methods of evaluation have encouraged an unstoppable tide of publications and grant proposals, many of which are poor quality. Many scientists are spending time on writing doomed proposals and papers when they would be better off engaging in research and scholarship in a less frenetic and more considered manner. But they won't do that so long as the pressures are on them to bring in grants and generate publications. I'll conclude with a few thoughts on how the system might be improved.

1. My first suggestions, regarding publications, are already adopted widely in the UK, but my impression is they may be less common elsewhere. Requiring applicants for jobs or fellowships to specify their five best publications rather than providing a full list rewards those who publish significant pieces of work, and punishes piecemeal publication. Use of the H-index as an evaluation metric rather than either number of publications or journal impact factor is another way to encourage people to focus on producing substantial papers rather than a flood of trivial pieces, as papers with low citations have no impact whatever on the H-index.There are downsides: we have the lag problem, which makes the H-index pretty useless for evaluating junior people, and in its current form the index does not take into account the contribution of authors, thereby encouraging multiple authorship, since anyone who can get their name on a highly-cited paper will boost their H-index, regardless of whether they are a main investigator or freeloader.

2. Younger researchers should be made aware that a sole focus on publishing in very high impact journals may be counter-productive. Rapid publication in an Open Access journals (many of which have perfectly respectable impact factors) may be more beneficial to ones career (http://openaccess.eprints.org/) because the work is widely accessible and so more likely to be cited. A further benefit of the PLOS journals, for instance, is that they don't impose strict length limits, so research can be properly described and put in context, rather than being restricted to the soundbite format required by very high impact journals.

3. Instead of using metrics based on grant income, those doing evaluations should use those based on efficiency, i.e. an input/output function. Two problems here: the lag in output is considerable, and the best metric for measuring output is unclear. The lag means it would be necessary to rely on track record, which can be problematic for those starting out in the field. Nevertheless, a move in this direction would at least encourage applicants and funders to think more about value for money, rather than maximising the size of a grant – a trend that has been exacerbated by Full Economic Costing (don't get me started on that). And it might make grant-holders and their bosses see the value of putting less time and energy into writing multiple proposals and more into getting a project done well, so that it will generate good outputs on a reasonable time scale.

4. The most radical suggestion is that we abandon formal institutional rankings (i.e. the successor to the RAE, the REF). I've been asking colleagues who were around before the RAE, what they think it achieved. The general view was that the first ever RAE was a useful exercise that exposed weaknesses in insitutions and individuals and got everyone to sharpen up their act. But the costs of subsequent RAEs (especially in terms of time) have not been justified by any benefit. I remember a speech given by Prof Colin Blakemore at the British Association for the Advancement of Science some years ago where he made this point, arguing that rankings changed rather little after the first exercise, and certainly not enough to justify the mammoth bureaucratic task involved. When I talk to people who have not known life without an RAE, they find it hard to imagine such a thing, but nobody has put forward a good argument that has convinced me it should be retained. I'd be interested to see what others think.

The difference between p < .05 and a screening test

Here's a fairly standard science story. A researcher compares a group of 30 children with autism/dyslexia/depression/chilblains and a matched control group on something: genotype/reactions to pharamaceuticals/behaviour profile/brain activation. A statistically significant difference is found between the groups. The result is published in a high profile journal.
The media want to know the relevance of this finding for their readers. It is not clear that this will lead to immediate treatment for autism/dyslexia/depression/chilblains, but they do feel justified in saying that the research will be useful in improving screening. After all, we all know that the earlier we can identify something, the easier it is to treat.

What's wrong with this? Well, alas, everything. And before going further, it is important to note that it is not just the media that get it wrong; many scientists blithely assert that their findings will have application in screening with no understanding of what is required to make a good screening test.

The four key considerations for a screening programme are take-up, costs, accuracy and intervention. Take-up can be surprisingly high, even for embarrassing and uncomfortable procedures. In the UK, most women go along with screening for cervical and breast cancer because, hey, having a total stranger introduce your private parts to cold metallic objects is, on balance, less bad than finding too late that you have a terminal disease.

But there are costs, of course. First, to the individual being screened, who has to take time out of a busy life to go along for screening, and second to the NHS, which must pay for the staff, equipment, facilities and infrastructure to do the screening. None of this is going to be worthwhile unless the screening is very accurate. If you are screening for cancer, then you cannot afford to make errors of omission: giving the all-clear when in fact the person has disease. But equally, you will be very unpopular if you make errors of commission – if you tell healthy person they have failed the screen, causing anxiety and leading them to have further tests that then fail to confirm the diagnosis. This has been a problem for the PSA screening test for prostate cancer.

Quite apart from the accuracy of diagnosis, the screening would not be worthwhile if the disorder you are screening for was not readily treatable – or preventable. There would be little point in identifying large numbers of people with disease X, even if you could do accurately, if nothing could be done about X. Indeed, it could be counterproductive.

In this light, let us consider recent stories in the media about using automated analysis of vocalisations to screen for autism. The study, by Oller and colleages, was published in Proceedings of the National Academy of Sciences in July 2010. It is an impressive and innovative study: the researchers had children wearing body-microphones so that all their utterances could be recorded, and they developed software that was able, with a high degree of accuracy, to distinguish the child's own utterances from those of other people and background noise. Using their extensive knowledge of the acoustic characteristics of babble and early language, they derived algorithms to characterise aspects such as pitch and rhythmic features in the vocalisations. They compared results for 106 typically-developing children, 77 children with autism and 49 children with language delay, and demonstrated that on a combination of these indices the groups were well discriminated. They concluded "We interpret this as a proof of concept that automated analysis can now be included in the tool repertoire for research on vocal development and should be expected soon to yield further scientific benefits with clinical implications." Screening is mentioned twice in the paper; in the abstract it states: "automated analysis should soon be able to contribute to screening and diagnosis procedures for early disorders", and in the introduction it is noted that autism is currently diagnosed mainly in terms of negative features, such as joint attention deficits and communication deficits and "abnormal vocal characteristics would constitute a positive marker that might enhance precision of screening or diagnosis." Note that these claims are pretty cautious: the vocal analysis is seen as 'contributing to' and 'enhancing precision' of screening. Nevertheless, the potential of the method as a screening tool has been emphasised in some media reports.

So how accurate is it? The key statistics for any screening instrument are sensitivity and specificity. Sensitivity is the proportion of 'hits', i.e. cases with autism who are correctly identified as having autism. Specificity is the proportion of 'true negatives', i.e, non-autistic children who are correctly identified as non-autistic. These two indices can only be defined in relation to a specific population, and their interpretation will depend crucially on the base rate of disorder in that population.

Oller et al reported identification of autism versus typical development showed sensitivity of 0.75 and specificity of 0.98. This corresponds to the situation shown below: 104/106 (98%) of typical children are accurately diagnosed, and 58/77 (75%) of autistic children are accurately diagnosed.

		Actual diagnosis
		Typical	Autistic	% autistic
Diagnosis	Typical	104	19
from vocal	Autistic	2	58
analysis	Total	106	77	42%

But their study sample was selected to contain a high proportion of children with autism, 42%. In the general population, rates of autism are much lower than this. The most liberal estimate, which includes children with far less severe problems than those included in this study, is around 1% (Baird et al, 2006). If we apply the sensitivity and specificity figures from Oller et al to a population with a base rate of autism of 1% - just by multiplying the number of typical children while keeping specificity constant – then the numbers look like this:

		Actual diagnosis
		Typical	Autistic	% autistic
Diagnosis	Typical	7471	19
from vocal	Autistic	152	58
analysis	Total	7623	77	1%

We see that in this simulated general population sample around three quarters of those who'd be diagnosed as autistic on the basis of vocal analysis are non-autistic. In reality, accuracy is likely to be lower than this in such a sample, because it would include children with milder cases of autism, including those with Asperger syndrome, who were excluded from the study by Oller et al.

It gets worse. A population sample would also include other non-autistic children with poor communication skills, including those with specific language difficulites, or conditions associated with more general developmental delay. Oller et al did include a non-autistic sample with language impairments, and it is clear from the presented data that there was considerable overlap between the autism and language impaired groups; my reading of the plotted data suggests around 43% of children with language impairment fell below the cutoff for abnormality on the vocal measures. The notion that vocal abnormality is a 'unique signature' for autism, as reported by some of the media, is clearly false.

Might there be situations where the vocal analysis could be clinically useful? Potentially, yes. Autism diagnosis is particularly difficult in young, low-functioning children, and even our gold-standard diagnostic tools can have difficulty distinguishing autism from non-autistic mental handicap in children under 18 months of age (Lord et al, 1993). The vocal measures of Oller et al might provide useful supplementary information in such cases, but bear in mind that the data presented so far suggest the vocal abnormalities can occur in conditions other than autism. Another context where the vocal analysis could be of value is in evaluation of very young children at high risk of autism, in particular young siblings of children with autism, around 10-20% of whom will develop autism or a related neurodevelopmental condition. It is possible that vocal analysis will be useful in identifying those likely to have problems. However, as noted by Zwaigenbaum et al (2006), even if we are able to identify such children early on, we then have to confront the fact that little is known about effective early intervention for autism. A further issue in the study of infant sibs is that vocal behaviours could be abnormal in such a sample if children imitate their older autistic sibling. Overall, automated vocal analysis could prove useful in early diagnosis of high risk groups, but we cannot be certain without further research. And even if we did find it could be used in this role, we would want to demonstrate that it provided information that could not be obtained by other simpler means. For instance, a brief parental questionnaire can be pretty effective in identifying autism (Berument et al., 1999).

Despite these caveats, I want to stress that I think the Oller et al study is an excellent piece of science. The method they have developed could provide important insights into the nature of communication problems in young children, and also be used to study how typical children learn to speak. It is a scholarly piece of work built on many years of painstaking research.

I've used the example of the Oller et al study because it provides a recent example of a good study whose clinical implications have been overstated, but there are many, many other instances. Take for instance, media coverage of findings of genes associated with risk for dyslexia. I just did so by Googling 'genes dyslexia screening', and found this article in the New York Times, which is typical of how genetic associations are reported in the media. The newspaper article states " Researchers said a genetic test for dyslexia should be available within a year or less. Children in families that have a history of the disorder could then be tested, with a cheek swab, before they are exposed to reading instruction. If children carry a genetic risk, they could be placed in early intervention programs". Now, I recently reviewed the research on genetic studies of dyslexia (Bishop, 2009). Even though I thought I knew the literature, I was pretty surprised by what I found. I looked at one of the more robust results in the field, on a gene called KIAA0319, described in a paper with the title " Strong evidence that KIAA0319 is a susceptibility gene for developmental dyslexia". The authors compared children with different haplotypes (allele combinations) in relation to dyslexia status. Here's my summary:

"The most common form with alleles 1–1 was equally frequent for affected versus unaffected cases, but two other common forms, 1–2 and 2–1, showed contrasting effects. (Conventionally, 1 is the more frequent allele, and 2 is the less frequent). The 1–2 haplotype was found in 35% of those with dyslexia and 27% of those without, whereas for 2–1, the figures were 24% in those with dyslexia and 36% in unaffected controls.... Extrapolating to the general population (i.e. taking base rates into account), one would expect that most individuals with the 1–2 risk haplotype would not be dyslexic, and most dyslexic individuals would not have the 1– 2 haplotype."

Note that, even without taking base rates into account, the strength of the association with genotypes is considerably lower than the Oller et al association between vocal behaviour and autism. This result causes excitement among geneticists because it has been replicated, and the evidence for association is strong in terms of p-values in a very large sample size. This finding potentially can tell us something about the development of brain regions that lead to risk for dyslexia, and it indicates that biology plays a role in dyslexia, and it is not just the result of poor parenting or poor teaching. But there is a difference between "strong evidence" and "strong effect": in fact, the effect size for individual genotypes is very small – far too small to play a useful role in screening. Since the 1970s we have had reasonably accurate ways of predicting which preschoolers are at risk for reading difficulties, based on simple behavioural tests and family background (see e.g. Satz & Friel, 1978). They are unlikely to be surpassed by any genetic tests in the foreseeable future.

Nevertheless, the belief that genes are destiny and are somehow more accurate than simple behavioural or observational measures in predicting problems is persistent. This encourages disturbing developments, such as firms offering genetic screening to identify your child's talents. Apparently you can pay to have your child tested for genes related to a host of personal characteristics, ranging from intelligence to optimism to dancing. Just one small problem: for many of these characteristics there is no published data linking gene variants to the trait. And for those that exist, the effects are tiny.

The arguments I present here are very old; I was taught about the importance of base rates by the late A. E. Maxwell when training as a clinical psychologist in 1975. However, knowledge of this aspect of epidemiology is not widespread, even among academic psychologists who are otherwise sophisticated users of statistics. I recently asked a group of MSc students if any of them knew about base rates, and they thought I was talking about the Bank of England.

So, the bottom line: just because someone finds a statistically significant difference between two groups, don't assume that will translate into a useful screening test.

(Red underline denotes corrections made 19th August 2010).

Cited references

Baird, G., Simonoff, E., Pickles, A., Chandler, S., Loucas, T., Meldrum, D., et al. (2006). Prevalence of disorders of the autism spectrum in a population cohort of children in South Thames: the Special Needs and Autism Project (SNAP). Lancet, 368 (9531), 210-215.

Berument, S. K., Rutter, M., Lord, C., Pickles, A., & Bailey, A. (1999). Autism screening questionnaire: Diagnostic validity. British Journal of Psychiatry, 175, 444-451.

Bishop, D. V. M. (2009). Genes, cognition and communication: insights from neurodevelopmental disorders. The Year in Cognitive Neuroscience: Annals of the New York Academy of Sciences, 1156, 1-18.

Lord, C., Storoschuk, S., Rutter, M., & Pickles, A. (1993). Using the ADI-R to diagnose autism in preschool children. Infant Mental Health Journal, 14, 234-252.

Satz, P., & Friel, J. (1978). Predictive validity of an abbreviated screening battery. Journal of Learning Disabilities, 11(6), 347-351.

Zwaigenbaum, L., Thurm, A., Stone, W., Baranek, G., Bryson, S., Iverson, J., et al. (2006). Studying the emergence of autism spectrum disorders in high-risk infants: Methodological and practical Issues. Journal of Autism and Developmental Disorders, 37, 466-480.

Further reading

Loong, T. W. (2003). Understanding sensitivity and specificity with the right side of the brain. (10.1136/bmj.327.7417.716). British Medical Journal, 327(7417), 716-719.

Postscript, 12^th August 2010

An article by Ecker et al that was published yesterday in Journal of Neuroscience comprehensively illustrates the points above.  The researchers gathered MRI brain scans on 20 adults with autism, 19 adults with ADHD, and 20 control adults with no neuropsychiatric diagnosis. Previous research has reported various differences between brains of people with autism and controls, but there have been few findings that are sufficiently strong and convincing to discriminate the groups. Indeed, it has been surprisingly difficult to find any consistent abnormalities on brain scanning, even in the case of children with severe impairments. Ecker et al adopted a different approach, by arguing that a constellation of features would be more effective than individual indices in distinguishing autism from control brains.

The three groups did not differ in terms of three measures of brain capacity: intracranial volume, total brain volume, and gray matter volume.

They used five measures to derive a 'classifier': an equation that puts the measures together in a way that maximally distinguishes the autism and control groups. These measures were (as far as I understand the highly technical account):

1. The average convexity or concavity of large-scale features of the brain surface. This measures sulcal depth and gyral height
2. Mean (radial) curvature. This assesses number of smaller convolutions on the surface of the brain.
3. A measure of the degree of cortical folding in terms of metric distortion relative to an average template.
4. Cortical thickness
5. Pial area, a measure of the grey matter surface.

To avoid the bias that can arise when the same data is used to derive and test a classifier, they adopted a 'leave one out' method, whereby one person with autism and one control were omitted when deriving the estimation of the equation. The resulting equation was then applied to classify the left-out cases. This was done separately for the left- and right sides of the brain.  Only the left-sided classifier was effective, giving the following results.

		Actual diagnosis
		Autistic	Control
Diagnosis	Autistic	18	4
from MRI	Control	2	16
classifier	Total	20	20

When the same left-hemisphere classifier was appplied to the ADHD group, the picture was similar. 4 of 19 cases were classified as autistic, and the remainder as non-autistic.

In the discussion of the results, the authors note the potential for clinical application as follows:

"... the existence of an ASD biomarker such as brain anatomy might be useful to facilitate and guide the behavioral diagnosis. This would, however, require further extensive exploration in the clinical setting, particularly with regards to classifier specificity to ASD rather than neurodevelopmental conditions in general. "

In other words, the classifier needs to be validated on other samples, and it is as yet unclear whether it would be as accurate if people with autism were contrasted, say, with people with language impairments. The authors also noted that the adult sample used here was largely composed of high-functioning adults with Asperger syndrome, and it was not clear whether results would generalise to other cases of autism.  In the final sentence of the paper it is stated: "classification values and specific patterns we report must be considered as preliminary".

In sum, the paper illustrates a promising approach to understanding more about brain development in autism, but it does not demonstrate the utility of this approach for differential diagnosis of autism from other conditions, nor for assisting diagnosis in marginal and difficult cases.

Encouraged by an enthusiastic press release from the Medical Research Council, who funded this work, the media picked up the story yesterday.  It was featured prominently on BBC television and radio news, made the front page story on the Independent, and was given extensive coverage in other national newspapers.  The account of the work showed little evidence of the caution and qualification in the published account.  In this case, I don't think the media can be blamed for misrepresenting the work, as much of what was said was taken from the MRC press release.  Here are some statements from the Independent, under the headline: "Brain scan promises to identify the hidden sufferers of autism":

• Autism could in future be diagnosed in 15 minutes from a brain scan

• Scientists ... have devised a method which can distinguish the autistic brain from the normal brain with 90 per cent accuracy.

• The method could lead to the introduction of screening for the disorder in children.

Dr Ecker was quoted as saying:

"The [computer programmme] says yes this is autism or no it is not, and also gives an indication of the severity."  She also contrasted the 15 minutes it took to do an MRI scan with conventional diagnostic procedures which "takes the whole day and involves asking embarrassing questions such as how many friends they have and how they are doing at school"

Dr Ecker seems to be implying that we should stop using diagnostic interviews to diagnose autism, because a brain scan is more accurate.  Since autism is currently defined in terms of a pattern of impairments in different domains of functioning, this is a remarkably bold claim, especially since her method awarded an autism diagnosis to 20% of controls.

Much is also made of the potential of the method for diagnosing autism in children. It's possible this may be effective, but children's brains are very different from adult brains, and one would need a whole new study to evaluate this. Furthermore, although Dr Ecker says of brain scanning "It doesn't hurt and you can even go to sleep", it is not an easy procedure to apply to young children without sedation.  Lying still in a very noisy tube is not something that comes naturally to a child, even if you can explain the procedure to them clearly so they know what to expect. Most children with autism have poor language comprehension and may also become anxious when in an unfamiliar situation. It is not impossible to do brain scanning studies with them, but it certainly is not easy.

A final thought. In recent years, brain research on autism has increased exponentially. There are other MRI datasets for adults and children with autism and other clinical groups as well as controls. It should be possible for Ecker and colleagues to cross-validate their findings fairly rapidly against other datasets. I hope that others will be willing to share their data to make this possible.

Book Review: The Invisible Gorilla

Chabris, C., & Simons, D. (2010). The invisible gorilla and other ways our intuition deceives us. London: HarperCollins. Psychology is a much misunderstood discipline. If you go into a high street bookstore, you will find the psychology section stuffed with self-help manuals and in all probability located next to the section on witchcraft and the occult. This is partly the fault of the Dewey Decimal Classification, which sandwiches Psychology firmly between Philosophy and Religion. For those who regard experimental psychology as a scientific discipline with affinities to medicine and biology this is a problem, and some psychology departments have dissociated themselves from the fluffy fringes of the discipline by renaming themselves as departments of cognitive science or behavioural neuroscience. An alternative strategy is to reclaim the term psychology to refer to a serious scientific discipline by demonstrating how experimentation can illuminate mental processes and come up with both surprising and useful results. This book does just that, and it does so in an engaging and accessible style. The book starts out with the phenomenon referred to in the title, and which the authors are best-known for, i.e. the Invisible Gorilla experiment. This has become well-known but I won't describe it in case the reader has not experienced the phenomenon. Richard Wiseman has a nice video demonstrating it. This is perhaps the most striking example of how we can deceive ourselves and be over-confident in our judgement of what we see, remember or know. In all there are six chapters, each dealing with a different 'everyday illusion' to which we are susceptible. My personal favourites were the last two chapters, which consider why people continue to believe in notions such as the damaging effect of MMR vaccination, or the beneficial effects of brain training for the elderly. Sceptics tend to dismiss those who persist such beliefs in the face of negative evidence, and denigrate them as stupid and scientifically illiterate. Chabris and Simons, however, are interested in why scientific evidence is so often rejected and consider why it is that anecdotes so much more powerful than data, and why we are sucked in to assuming there is causation when only correlation has been demonstrated. My one disappointment was that they did not say more about the reasons for wide individual variation in people's scepticism. After a rigorously sceptical undergraduate course in experimental psychology at Oxford, I assumed that all my peers on the course would be sceptics through-and-through, but that is far from being the case: I have intelligent friends who learned all about the scientific method, just as I did, yet who now are adherents of alternative therapies or psychoanalysis. I find this deeply puzzling, but it makes me realise that the satisfaction I find in the scientific method is in part due to the fact that it resonates with the way my brain works, and there are others for whom this is not so. In sum, I enjoyed this book for the insights it gave into how people think and reason, and for its emphasis on the need to adopt scepticism as a mind-set. Its avoidance of jargon and clear explanations give it broad appeal, and it would make an ideal text for undergraduates entering the field of experimental psychology, because it illustrates how a good experimenter thinks about evidence and designs studies to test hypotheses.

An exciting day in the life of a scientist

or: How to kill a few hours trying to get publication quality figures out of Matlab This is really just a boring moan; blogging as therapy. Well, yesterday I had the excitement of getting proofs for an 'in press' article. Virtually no errors to be corrected, but what was this list of queries from the publisher? Ah, the figures. Resolution too low. Well, that should be easy to fix - I'd do it first thing. Or so I thought. 9.30 a.m. The paper has an unusually large number of figures, eight, some in colour. All were created in Matlab and saved as .tiff format. I was pretty proud of generating the figures in Matlab. Graphics in Matlab is a bit of a nightmare and takes some time to learn, but once learned, you can generally create figures that are more complex than those produced by the other applications that I know. The proofs have come from Developmental Science, but they tell me the figures are too low resolution, even though I'd selected a 'no compression' option when saving them. Coincidentally, I have another article that is under consideration by Journal of Neuroscience, who also mention their stringent requirements for figure quality, and point me to a website, Cadmus, that will explain what is required and how to do it. Oh good, I think. Someone will help walk me through how to get good quality figures. Ha ha ha. Cadmus has a list of programs and formats that are supported. Alas, Matlab not among them. But Adobe Illustrator is. We have a copy of that. I used to have it on my machine, but uninstalled it, because I never used it and I got fed up when graphics files defaulted to opening in it, which took ages. Tracked down the CD, reinstalled it (compact version). Right, I think, Matlab will allow me to export a file in .ai format, and then I will be OK. Ha ha ha 9.45 I start with the simplest figure I have – a simple black and white line drawing with a couple of text labels. I save it with .ai format. When I click on it, Adobe Illustrator tries to open it, but first tells me it has 'unrecognised fonts' (Arial?) and then says it can't open it. OK, I think. But I can open an .eps or .tiff file in Adobe, and I can also save my Matlab figure in those formats. But once again, I get strange messages about wrong fonts, and for the .eps version, what appears on the screen is unrecognisable from the original. I look again at what Cadmus says about Adobe Illustrator. Oh dear. "PLEASE NOTE: When creating graphics in illustration programs such as Adobe Illustrator with the intention of outputting to an imagesetter or platesetter, it is extremely important that the person creating the illustration have a thorough understanding of the details of imaging in a prepress environment. There are an abundance of complex problems that can occur at output if paths are set up improperly, colors are indicated incorrectly, or other elements are constructed improperly. Trapping issues can also present problems if not addressed. The more complicated your illustration becomes, the greater the probability of problems at output, and therefore the need for more expertise and experience in creating the files." Decide that I had better try another option, since I have never used Adobe Illustrator and would not recognise a platesetter if I stumbled over one. But, I think, there is a helpful application associated with Cadmus that allows you to check your files. And I can just open my .eps file from there. Having gone through the usual round of registering, thinking of a password, getting email confirmation of the account, etc. I am in to 'Rapid Inspector'. I try opening my .tiff file. FAIL says Rapid Inspector. Resolution too low. OK, how about .eps version? Ah, says Rapid Inspector"Rapid Inspector found an image with CMYK color. CMYK color is not supported. Acceptable color space include(s): Spotcolor, Lineart, Grayscale, RGB." But this is a black and white figure! I spend some time in Matlab trying to sort this one out, but with no success. My own fault, but I can't find the script that I made to generate the figure in the first place, and I will need to redo it with different fonts etc. So waste 10 mins tracking it down and resolving once again always to save my programs in sensible places with sensible names. I go on to the web to find out how to change the colormap to gray. Re-run program, save the figure, and try it again in Rapid Inspector. It still tells me I have CMYK color. It also complains about my fonts. "Rapid Inspector detected that some or all fonts are missing from this file. To pass inspection, all fonts must be embedded. The following fonts are not embedded: Helvetica. " That's odd, as I was using Arial, not Helvetica. Try a few more runs of the program with different fonts. It still doesn't like my fonts. 10.45 Time to do a Google search about how to save a Matlab figure with embedded fonts. Well, it is nice to know I am not alone, and that many others have had this problem over the years. Several complain that it is about time Matlab did something about it. One helpful person, Oliver Woodford, has written a routine called export_fig, which is freely available: http://www.mathworks.com/matlabcentral/fileexchange/23629 Excellent. But, he explains, if you want to use it to create the kinds of files I need, you need to download two other applications from other sources. Fortunately, I already have the first, but the second, xpdf, is one of those applications that makes the non-geek's heart sink when you go to the download webpage and find, instead of clear instructions about what to do, a whole list of possibilities. I fear that the one I probably need ends in .tar.gz. I've tangled with these things before but can never quite remember what to do with them. 11.30 After a bit of fiddling about, I save the .tar.gz file, then try to extract the contents. A few failures as I do something wrong, and then at last I have it. But I am not sure I have it in the right place and no indication is given as to where it should be saved. I've just stuck in my Matlab program folder. 12.00 OK I should be all set, so now let's look at the examples of how to use export_fig. Nice helpful man who wrote the script clearly has been through everything I have, and more. He writes: "Exporting a figure from MATLAB the way you want it (hopefully the way it looks on screen), can be a real headache for the unitiated, thanks to all the settings that are required, and also due to some eccentricities (a.k.a. features and bugs) of functions such as print. The first goal of export_fig is to make transferring a plot from screen to document, just the way you expect (again, assuming that's as it appears on screen), a doddle." This is looking more promising.... Print out the instructions – 13 pages of them. 12.30 Took a break to look at some interesting data: what I ought to be doing instead of this rubbish. 14:30 OK back to export_fig. First attempt failed. Matlab can't find export_fig. I need to put the script somewhere else. OK,eventually sorted that by putting all the export_fig m files onto the Matlab folder in My Documents. All going very well so long as I am exporting to .png format. But I want .eps. When I try that the program complains it needs pdftops . SO where the hell is that? I will have a hunt. Found it, but it is a .cc file. does not seem to be recognised by matlab. So I have now spent more time on the website looking for a .m file. Doesn't appear to be one. Gave up and decided to try a .tiff file. Hah! nasty bossy Rapid Inspector says PASS. Hooray! But turned out I was reading in a different file created with the same name in May. Back to my .tiff option in export_fig This fails resolution test, even though it is specified as max quality. 15.00 Have a cup of tea. Back to trying the .eps option. Can't work out how to use the xpng file. Program stops and asks for pdftops. I have located pdftops.m and pdftops.cc but neither seems what it wants. As far as I can see from looking at the code, it wants an .exe file. The web tells me that a .cc file is a C++ file. In some desperation I tried renaming the .cc file as .exe, but that did not work. Decide to write to the author of the script, having read all the comments on the program and found that nobody else is having problems. Send the email. It bounces. I had mistakenly included a full stop at the end of the email address. Try to resend to correct address: email keeps autocompleting to the address with the full stop. After 2 tries, get into 'frequent contacts' in address book and delete entry so can now send the email. 15.35. I need another cup of tea to calm down. So now trying figure 2 , coloured headplot. Already have as .tiff; it looks very nice. Rapid inspector tells me FAIL! resolution is too low. I try saving as .png. Get lovely looking picture. Rapid inspector won't read it. Try exporting from microsoft image reader to .tiff and then reading in. Now I get: "alpha_planes: Rapid Inspector found extra color channels within this image. Extra color channels are also known as Alpha channels. Alpha channels are not supported. Please use an image editor to remove alpha channels from this file.resolution: Rapid Inspector found a low-resolution (RGB) image (96 DPI). The minimum required resolution for this type of image is 300 DPI. " 16:30 The wonderful Oliver Woodford replied and explained patiently how to cope with the pdftops thing. I downloaded. Still did not work. Downloaded again to the location he had said his was in . It works!! And the figures it creates are acceptable to the wretched Rapid Inspector. Verdict I'm really grateful for those who have produced free software that helped me deal with this. But I am really annoyed on two counts. First, Matlab is an expensive package. It does wonderful things and I love it to bits as a programming tool, but its graphics are not easy to use. People have been complaining for at least 2 years about the difficulty of generating high resolution output, yet nothing has been done. It should be high priority for the Matlab developers to fix this so that there is a simple command to generate this kind of output. Second, the Journal of Neuroscience exemplifies a trend in many journals to make authors do a lot of work that would, in the old days, have been done by copy-editors and other professionals. Scientists are supposed to have skills in graphic design and programming on top of all their other accomplishments. Some journals do still accept figures in a range of formats and look after any conversion from their end. But increasingly, the onus is put on authors. There appears to be no correlation between the wealth of a journal and the amount of help it will give to authors – in fact, if there is a correlation, I suspect it is inverse. Journal of Neuroscience charges hefty fees for just submitting a paper, let alone publishing it, with added costs of $1000 per figure unless first and last authors are members of the Society for Neuroscience – we are not and we have lots of colour figures. So our grant will be spent on shoring up J. Neuroscience rather than employing a vacation student for a few weeks. I reckon that on a 1-10 scale of geekiness I am a 6-7, and I am struggling. I am a full-time researcher with good support. I am a reasonable programmer. But I've got lots of colleagues who are trying to produce papers who are closer to a 1 or 2 on the geekiness scale, have little or no support, and are trying to fit research around busy teaching commitments. How on earth can they cope with all of this?

Journalists and the "scientific breakthrough"

There has been some animated discussion about science journalism by journalists and bloggers relating to the Fish Oil story that featured in my 1st June blog on the Orwellian prize. In summary, Ben Goldacre wrote a piece criticising the lax journalism behind the story, and was then roundly criticised himself by Jeremy Laurance of the Independent, who felt Ben was going too far in attacking hard-pressed journalists. There is a good piece by Ed Yong that gives the background and offers a cogent analysis. Here I don't want to rehearse the arguments – I've already added a comment to Yong's blog underlining my support for Ben Goldacre. Instead I have a constructive suggestion from a scientist to science journalists about how they might do things differently when handling science stories. This is prompted by my experiences when attending meetings of the British Science Festival. The British Science Association, which runs the festival, has a distinguished track record: founded in 1831 as the British Association for the Advancement of Science, its meetings included highlights such the first use of the term 'dinosaur' (1841), the debate on Darwinism between Huxley and Wilberforce (1860), Joule’s experiments (1840s) and the first demonstration of wireless transmission (1894). Times, however, have changed. Science has become increasingly specialised. The British Science Festival plays a key role in fulfilling the stated goals of the Association: "connecting science with people: promoting openness about science in society and affirming science as a prime cultural force through engaging and inspiring adults and young people directly with science and technology, and their implications". It is, however, not a venue where scientists reveal to the world a hitherto unreported "breakthrough". In general, the material that is reported at the Festival will either be already published in specialist journals, or will be "work in progress". In fact, most scientists find the whole concept of the "breakthrough" suspect: most research proceeds incrementally rather than by a sudden leap forward. The media, however, don't seem to grasp this essential point. They descend on the meeting in droves where they summon presenters to press conferences based on the one-paragraph press releases that the scientists are encouraged to supply. They don't attend the lectures. If my experience is anything to go by, they focus on at most 5% of the presentations, selecting those that they judge will make a good story of interest to the general public. Then during the week of the Festival, there is a plethora of newspaper articles which report on the selected presentations, inevitably talking about them as if the work is entirely new. Scientists then get uncomfortable as they feel their research has been "talked up" to make it into a newsworthy "breakthrough". The following week, the newspaper coverage of science reverts to its previous low level. Now, while I can understand some of the reasons for this, it seems to me a terrific waste of an opportunity. Gathered at the Festival is a subset of Britain's scientific elite, selected in large measure because they are doing interesting research and can communicate their science to a general audience. (Inevitably there are some who are hopeless at doing this and misunderstand the nature of the audience, but they are a minority). Their work doesn't stop when the Festival comes to an end. They will return to their labs and continue doing the interesting research. So if I were a science journalist, I would go to the Festival not to frenetically write stories to be published that week, but to make contacts with researchers who could supply me with good science stories for the rest of the year. I'm sure most journalists don't have time to tour the country interviewing scientists, but if they could make a personal contact with a scientist and persuade them they want to write a serious piece, they would find most would be amenable to a future telephone interview. And instead of having to respond rapidly to a press release, journalists could take a more relaxed approach, which would reduce their stress levels and give them time to check things carefully. I suspect that many journalists will reply to say this is all very well, but it's not news and so editors would not stand for it. Their job is not to provide the public with a general science education, but to tell people about breakthroughs. I disagree. There is far too much science for any one person to grasp, and so most scientific research will be novel to the majority of readers. The difficulty is to explain what is often technical and complex material to a lay readership. We have some excellent science journalists who are good at doing exactly that. If they could build up a network of relationships with scientists, they'd find a great many fascinating stories out there that are currently appreciated by only a minority of specialists.

Book review: biography of Richard Doll

Smoking kills: the revolutionary life of Richard Doll by Conrad Keating Signal Books: Oxford, 2009 I only once had the opportunity of hearing Richard Doll speak. It was in 2004, after a hard-hitting lecture by Charles Warlow on over-regulation of research (http://tiny.cc/m1n7v). Doll, aged 92, looking physically frail but mentally alert, stood up to point out that under current ethics regulation, none of the epidemiological studies that he had done to demonstrate a link between smoking and cancer would have been possible. The only way to rescue epidemiology from the trend for increasingly strict and bureaucratic constraints, he felt, was for someone to deliberately flout the law and be prepared to go to prison for the cause of liberating research. "I am prepared to volunteer myself for that role", he said, prompting a spontaneous outburst of applause. This engaging biography of Doll paints a picture of a man who could have been trusted to follow through on this offer. But as well as telling us about the remarkable life of Doll himself, the book is fascinating for its account of the history of evidence-based research in medicine. Doll would have gone to Cambridge to read mathematics were it not for the fact that he flunked one of the examinations after being plied with strong alcohol the night before. That fateful event led him to study medicine at St Thomas's Hospital, but he never lost his love of mathematics, and was quick to see the potential for using statistical methods and randomisation to evaluate treatments. Together with Austin Bradford Hill he developed the method of randomised controlled medical trials which has become the cornerstone for evaluation of efficacy of treatments. He subsequently took up a post researching disease prevention, a niche that not only suited him well, but was also one of the few options open to him, as his membership of the Communist party made him virtually unemployable as a hospital doctor. Remarkably, Home Office regulations meant he was also banned from teaching undergraduates, although he was allowed to teach postgraduate students. The account of his seminal work on smoking and cancer was a revelation to me. I had no idea that in the 1950s it was commonplace for doctors to offer a cigarette to a patient to calm them down before an examination. Nor that there had been a six-fold increase in lung cancer mortality in males between 1930 and 1944. Many of the discussions around this epidemic are reminiscent of those currently seen in the field of autism – was there some factor that could explain the increase, or was it simply that detection of the disease had improved, especially with new X-ray methods for visualising tumours? Doll was remarkable for his single-mindedness and energy in assessing large numbers of patients, and for his ability to see the need for controls. He was ever alert to the possibility of misinterpreting data and developed methods of guarding against unwitting bias. Calculations were done by hand and painstakingly checked. Doll was concerned not to publish until certain of his facts, leading to some delay in publication of the first results. Keating emphasises the extent to which Doll felt it important not to become a campaigner for public health measures, but merely to present the results of his findings. It is a view nicely summed up by a comment attributed not to Doll, but to his collaborator Hill, who was confronted at a cocktail party by a doctor who said "You're the chap who wants us to stop smoking." "Not at all," replied Hill. "I'm interested if you go on smoking to see how you die." As each new study by Doll found further support for a strong link between smoking and lung cancer, and also revealed an unexpected link with heart disease, initial apathy towards the results turned into acceptance by the Medical Research Council, criticism by the tobacco industry, who derided the findings as 'unscientific', and alarm by the government, who made substantial sums in taxes on smoking. One of the harshest critics was the eminent statistician and heavy smoker R. A. Fisher. Fisher was exercised by a key limitation of epidemiological studies, the lack of experimental control. "Correlation does not mean causation" was his mantra, and he argued forcefully for alternative explanations of the association. The debate turned acromonious, with Fisher accusing Doll and Hill of failure to make their data available, and others accusing Fisher of conflict of interest, owing to his lucrative consultancies with tobacco companies. Again, aspects of the debate have some modern resonances: in my own field of neuropsychology, it is often argued that the goal is to find the necessary and sufficient cause of a disorder, much as Fisher had argued. On this view even a single case of lung cancer in a non-smoker could overturn a causal theory. But gradually it became clear that a factor such as smoking could act as a risk factor for disease without acting in a deterministic fashion. In my own writings on developmental neuropsychology I have used the example smoking and cancer to make the point that causal mechanisms may be multifactorial and probabilistic (http://tiny.cc/i8x5l), but until I read this book I had not realised that there was a bitter debate around this very issue in the 1950s. Keating describes it as a shift from reliance on Koch's postulates to Hill's specification of criteria for causality. Koch, working on infectious diseases had specified that, among other things, to prove an organism was the cause of a disease the organism had to be discoverable in every instance of the disease, and that experimental animals could be given the disease by inoculation with a pure culture. Hill's criteria involved nine viewpoints, none of which on its own gave indisuptable evidence for a causal effect, but which taken together would help determine whether causality was a reasonable hypothesis: strength, consistency, temporality, biological gradient, plausibility, coherence, experiment and analogy. Doll is best-known for his work on smoking, but he also played a pivotal role in discovering the health risks of asbestos, ionising radiation and the contraceptive pill. Keating tackles head-on the accusations that emerged after Doll's death that he was in the pay of companies such as ICI and Monsanto, and refutes firmly any suggestion of malpractice. Doll believed that if one wanted to obtain access to data it was important to have some relationship with companies. This emerged most strikingly in his early work on asbestos, where his preliminary findings caused shock and alarm. He resisted attempts to suppress the data, but negotiated with the company where he had done his studies with the aim of doing further analyses. The company were willing to implement changes to their working practices and Doll judged that more good could be done by working with them than attacking them: after Doll's findings, measures for containing asbestos fibres were taken so that the workers could at last see that there was a clock on the far-side wall. Doll made no personal profit from this company, nor from his work for chemical firms, whose fees were donated to charity. Nevertheless, the book raises big questions about how to handle potential conflict of interest and illustrates the importance of modern practices of full disclosure – which only became commonplace after his retirement, and of which Doll fully approved. I can thoroughly recommend this book as providing a stimulating account of a fascinating life. It puts into historical perspective aspects of medical statistics and epidemiology that are now largely taken for granted, but which may have taken much longer to be developed without Doll's intelligence and dedication. A final word of thanks to the Book House, Summertown, the small, independent bookseller where I happened upon this book. Please support them if you live in Oxford: I can guarantee that if you wander in and have a browse, you will find something interesting and unexpected on the shelves. (And no, I don't have any vested interests – just keen for the survival of a local amenity!)

Orwellian prize for journalistic misrepresentation

CALL FOR NOMINATIONS


I am offering a prize each year for an article in an English-language national newspaper that has the most inaccurate report of a piece of academic work.

The prize will consist of a certificate and statuette and I would welcome suggestions for the design of both of these

.

The prize will be awarded in January of each year.

Rules

1. The article must purport to report results of academic research, and judgement will be based on a points scoring system, as follows:

    * Factual error in the title: 3 points
    * Factual error in a subtitle: 2 points
    * Factual error in the body of the article: 1 point

2. Factual errors must be ones that can be judged against publicly available documents – i.e. not just opinions or reports of interviews.

3. Nominations must be posted on this blog. The nomination should contain:

    * Web addresses for both the nominated article and the academic source that is misrepresented.
    * Name and email contact of the nominator. Anonymous nominations are not allowed
    * A scored copy of the article, as illustrated below

If a nominated article is not available electronically, then the nominator should provide a list of the points used to score the article, and retain a photocopy of the article, which should be provided to the judges on request.

4. If there is more than one plausible candidate for the prize, then additional criteria will be used, such as:

    * The seriousness of the error, e.g. could it damage vulnerable groups?
    * Relevant undisclosed vested interests by journalist or his/her newspaper
    * The ratio of accurate to inaccurate content
    * The presence of irrelevant but misleading content
    * The size of the readership

and mitigating circumstances, such as

    * Whether there was a misleading press release from the academic's institution
    * Whether a scientist colluded in 'talking up' the findings and going beyond data

Nominators are encouraged to comment on these points also, but final judgement will be made by a panel of judges.

Illustrative example of nomination:

The following article is a strong contender for the prize in 2010, and illustrates the scoring system.

Inaccurate sections shown in square brackets with N points in round brackets.

Nominated article: http://www.guardian.co.uk/science/2010/may/30/fish-oil-supplement-concentration

Misrepresented source article: http://www.ajcn.org/cgi/content/abstract/91/4/1060

Nominator: DVM Bishop, dorothy.bishop@psy.ox.ac.uk

[Fish oil](3) helps schoolchildren [to concentrate](3)

US academics discover [high doses of omega-3 fish oil](2) combat [hyperactivity and attention deficit disorder](2)

* Denis Campbell

* The Observer, Sunday 30 May 2010

Children [can learn better at school](1) by taking [omega-3 fish oil supplements](1) which [boost their concentration](1), scientists say.

Boys aged eight to 11 who were given doses [once or twice a day](1) of docosahexaenoic acid, an essential fatty acid known as DHA, showed [big improvements in their performance during tasks involving attention](1).

Dr Robert McNamara, of the University of Cincinnati, who led the team of American researchers, said their findings could help pupils to study more effectively and potentially help to tackle both attention deficit hyperactivity disorder (ADHD) and depression. The study, reported in the American Journal of Clinical Nutrition, is important because a lack of DHA has been implicated in ADHD and other similar conditions, with poor maternal diet sometimes blamed for the child's deficiency.

ADHD affects an estimated 4%-8% of Britons and can seriously impair a child's education because they have trouble concentrating and are often disruptive in class. A lack of DHA has also been associated with bipolar disorder and schizophrenia.

"We found that, if you take DHA, you can enhance the function of those brain regions that are involved in paying attention, so it helps people concentrate," said McNamara. "The benefit is that it may represent an intervention that will help children or adults with attention impairments."

The researchers gave 33 US schoolboys 400mg or 1,200mg doses of DHA or a placebo every day for eight weeks. [Those who had received the high doses did much better in mental tasks involving mathematical challenges](1). Brain scans showed that functional activity in their frontal cortex – which controls memory, attention and the ability to plan – increased significantly.

The results, and fact that many people eat too little fish to get enough DHA through their diet, meant it could help all children to improve their learning, added McNamara. "The primary benefit is to treat ADHD and depression, but it could also help people with their memory, learning and attention," he said.

--------------------------------------------------------------------------------------------------------------------

12th September 2010

New nomination by Jon Simons, who has pointed out to me that there is a word limit on Comments, which makes it difficult to post nominations there. If you have a nomination, please save as a text file and send to me (email above) and I can post it here.

Nominated article:

http://www.washingtonpost.com/wp-dyn/content/article/2010/09/09/AR2010090904116.html

Original article: http://www.sciencemag.org/cgi/content/abstract/329/5997/1358

Nominator: Jon Simons (jss30@cam.ac.uk)

Scientists can [scan brains for maturity](3), potentially [gauging child

development](3)

By Rob Stein, Washington Post Staff Writer, Thursday, September 9, 2010; 6:13 PM

Scientists have developed a scan that can [measure the maturity of the brain](1), an advance that someday might be useful for [testing whether children are maturing normally](1) and for [gauging whether teenagers are grown-up enough to be treated as adults](1).

A federally funded study that involved [scanning more than 12,000 connections](1) in the brains of 238 volunteers ages 7 to 30 found that the technique appeared to accurately differentiate between the brains of adults and children and determine roughly where individuals scored in the normal trajectory of brain development.

 While much more work is needed to validate and refine the test, the technique could have a host of uses, including [providing another way to make sure children's brains are developing properly](1), [in the same way doctors routinely measure other developmental milestones](1). [The scan could, for example, identify children who might be at risk for autism, schizophrenia and other problems because their brains are not maturing normally](1).

"If you are worried about a kid's development, in five minutes you could do a scan and it would spit out a measurement of their brain maturity level," said Nico Dosenbach, a pediatric neurology resident at St. Louis Children's Hospital who helped develop the technique described in Friday's issue of the journal Science. "That's sort of the future."

The technique developed by Dosenbach and his colleagues uses magnetic resonance imaging, already commonly used to measure activity in the brain by correlating increases and decreases in [blood flow](1) to various brain regions. The scans are considered safe because they do not use radiation.

In this case, the technique was called functional connectivity magnetic resonance imaging, or fcMRI, because it [measured connections](1) in the resting brains of the subjects. The researchers used a computer program to analyze how [connections in the brain changed as the mind matured](1), pinpointing 200 to produce an index of maturity. They found that [close connection weakened while distant connections strengthened as the brain matures](1), until about age 21 or 22.

Dosenbach estimated they were able to distinguish between the brain of children ages 7 to 11 and that of adults ages 25 to 30 with 90 percent accuracy. They were able to differentiate between adolescents and adults with 75 percent accuracy, Dosenbach said in an e-mail.

But Dosenbach warned that it would be premature to start using the technique to measure individual maturity levels.

"I would not endorse that," he said.