Open code: not just data and publications

I had a nice exchange on Twitter this week.

Nick Fay had found a tweet I had posted over a year ago, asking for advice on an arcane aspect of statistical analysis:

I'd had some replies, but they hadn’t really helped. In the end, I’d worked out that there was an error in the stats bible written by Rand Wilcox, which was leading me astray. Once I’d overcome that, I managed to get the analysis to work.

It was clear Nick was now having the same problem and going round in exactly the same circles I had experienced.

My initial thought was that I could probably dig out the analysis and reconstruct what I’d done, but my heart sank at the prospect. However, then I had a cheerful thought. I had deposited the analysis scripts for my project on the Open Science Framework, here. I checked, and the script was pretty well annotated, and as a bonus you got a script showing you how to make a nice swarm plot.

This experience comes hard on the heels of another interaction, this time around a paper I’m writing with Paul Thompson on p-curve analysis (latest preprint is here). Here there’s no raw data, just simulations, and it’s been refreshing to interact with reviewers who not only look at the code you have deposited, but also make their own code available.  There’ve been disagreements with the reviewers about aspects of our paper, and it helped enormously that we could examine one another’s code. The nice thing is that if code is available, you get to really understand what someone has done and also learn a great deal about coding.

These two examples illustrate the importance of making code open. It probably didn’t matter much when everyone was doing very simple and straightforward analyses. A t-test or correlation can easily be re-run from any package given a well-annotated dataset. But the trend in science is for analyses to get more and more complicated. I struggle to understand the methods of many current papers in neuroscience and genetics – fields where replication is sorely needed but impossible to achieve if everyone does things differently and only incompletely described. Even in less data-intensive areas such as psycholinguistics, there has been a culture change away from reliance on ANOVAs to much more fancy multilevel modelling approaches.

My experience leads me to recommend sharing of analysis code as well as data: it will help establish reproducibility of your findings, provide a training tool for others, and ensure your work is in a safe haven if you need to revisit it.

Finally, this is a further endorsement of Twitter as an academic tool. Without Twitter I wouldn't have discovered Open Science Framework, or PeerJ, both of which are great for those who want to embrace open science. And my interchange with Nick was not the end of the story. Others chipped in with helpful comments, as you can see below:

P.S. And here is another story of victory for Open Data, just yesterday, from the excellent Ed Yong.

Who's afraid of Open Data

Cartoon by John R. McKiernan, downloaded from: http://whyopenresearch.org/gallery.html

I was at a small conference last year, catching up on gossip over drinks, and somehow the topic moved on to journals, and the pros and cons of publishing in different outlets. I was doing my best to advocate for open access, and to challenge the obsession with journal impact factors. I was getting the usual stuff about how early-career scientists couldn't hope to have a career unless they had papers in Nature and Science, but then the conversation took an interesting turn.

"Anyhow," said eminent Professor X. "One of my postdocs had a really bad experience with a PLOS journal."

Everyone was agog. Nothing better at conference drinks than a new twist on the story of evil reviewer 3.  We waited for him to continue. But the problem was not with the reviewers.

"Yup. She published this paper in PLOS Biology, and of course she signed all their forms. She then gave a talk about the study, and there was this man in the audience, someone from a poky little university that nobody had ever heard of, who started challenging her conclusions. She debated with him, but then, when she gets back she has an email from him asking for her data."

We wait with bated breath for the next revelation.

"Well, she refused of course, but then this despicable person wrote to the journal, and they told her that she had to give it to him! It was in the papers she had signed."

Murmurs of sympathy from those gathered round. Except, of course, me. I just waited for the denouement. What had happened next, I asked.

"She had to give him the data. It was really terrible. I mean, she's just a young researcher starting out."

I was still waiting for the denouement. Except that there was no more. That was it! Being made to give your data to someone was a terrible thing. So, being me, I asked, why was that a problem? Several people looked at me as if I was crazy.

"Well, how would you like it if you had spent years of your life gathering data, data which you might want to analyse further, and some person you have never heard comes out of nowhere demanding to have it?"

"Well, they won't stop you analysing it," I said.

"But they may scoop you and find something interesting in it before you have a chance to publish it!"

I was reminded of all of this at a small meeting that we had in Oxford last week, following up on the publication of a report of a symposium I'd chaired on Reproducibility and Reliability of Biomedical Research. Thanks to funding by the St John's College Research Centre, a small group of us were able to get together to consider ways in which we could take forward some of the ideas in the report for enhancing reproducibility. We covered a number of topics, but the one I want to focus on here is data-sharing.

A move toward making data and analyses open is being promoted in a top-down fashion by several journals, and universities and publishers have been developing platforms to make this possible. But many scientists are resisting this process, and putting forward all kinds of argument against it. I think we have to take such concerns seriously: it is all too easy to mandate new actions for scientists to follow that have unintended consequences and just lead to time-wasting, bureaucracy or perverse incentives. But in this case I don't think the objections withstand scrutiny. Here are the main ones we identified at our meeting:

1.  Lack of time to curate data;  Data are only useful if they are understandable, and documenting a dataset adequately is a non-trivial task;

2.  Personal investment - sense of not wanting to give away data that had taken time and trouble to collect to other researchers who are perceived as freeloaders;

3. Concerns about being scooped before the analysis is complete;

4.  Fear of errors being found in the data;

5.  Ethical concerns about confidentiality of personal data, especially in the context of clinical research;

6.  Possibility that others with a different agenda may misuse the data, e.g. perform selective analysis that misrepresented the findings;

These have partial overlap with points raised by Giorgio Ascoli (2015) when describing NeuroMorpho.Org, an online data-sharing repository for digital reconstructions of neuronal morphology. Despite the great success of the repository, it is still the case that many people fail to respond to requests to share their data, and points 1 and 2 seemed the most common reasons.

As Ascoli noted, however, there are huge benefits to data-sharing, which outweigh the time costs. Shared data can be used for studies that go beyond the scope of the original work, with particular benefits arising when there is pooling of datasets. Some illustrative examples from the field of brain imaging were provided by Thomas Nichols at our meeting (slides here), where a range of initiatives is being developed to facilitate open data. Data-sharing is also beneficial for reproducibility: researchers will check data more carefully when it is to be shared, and even if nobody consults the data, the fact it is available gives confidence in the findings. Shared data can also be invaluable for hands-on training. A nice example comes from Nicole Janz, who teaches a replication workshop in social sciences in Cambridge, where students pick a recently published article in their field and try to obtain the data so they can replicate the analysis and results.

These are mostly benefits to the scientific community, but what about the 'freeloader' argument? Why should others benefit when you have done all the hard work? In fact, when we consider that scientists are usually receiving public money to make scientific discoveries, this line of argument does not appear morally defensible. But in any case, it is not true that the scientists who do the sharing have no benefits. For a start, they will see an increase in citations, as others use their data. And another point, often overlooked, is that uncurated data often become unusable by the original researcher, let alone other scientists, if it is not documented properly and stored on a safe digital site. Like many others, I've had the irritating experience of going back to some old data only to find I can't remember what some of the variable names refer to, or whether I should be focusing on the version called final, finalfinal, or ultimate. I've also had the experience of data being stored on a kind of floppy disk, or coded by a software package that had a brief flowering of life for around 5 years before disappearing completely.

Concerns about being scooped are frequently cited, but are seldom justified. Indeed, if we move to a situation where a dataset is a publication with its own identifier, then the original researcher will get credit every time someone else uses the dataset. And in general, having more than one person doing an analysis is an important safeguard, ensuring that results are truly replicable and not just a consequence of a particular analytic decision (see this article for an illustration of how re-analysis can change conclusions).

The 'fear of errors' argument is, of understandable but not defensible. The way to respond is to say of course there will be errors – there always are. We have to change our culture so that we do not regard it as a source of shame to publish data in which there are errors, but rather as an inevitability that is best dealt with by making the data public so the errors can be tracked down.

Ethical concerns about confidentiality of personal data are a different matter. In some cases, participants in a study have been given explicit reassurances that their data will not be shared: this was standard practice for many years before it was recognised that such blanket restrictions were unhelpful and typically went way beyond what most participants wanted – which was that their identifiable data would not be shared.  With training in sophisticated anonymization procedures, it is usually possible to create a dataset that can be shared safely without any risk to the privacy of personal information; researchers should be anticipating such usage and ensuring that participants are given the option to sign up to it.

Fears about misuse of data can be well-justified when researchers are working on controversial areas where they are subject to concerted attacks by groups with vested interests or ideological objections to their work. There are some instructive examples here and here. Nevertheless, my view is that such threats are best dealt with by making the data totally open. If this is done, any attempt to cherrypick or distort the results will be evident to any reputable scientist who scrutinises the data. This can take time and energy, but ultimately an unscientific attempt to discredit a scientist by alternative analysis will rebound on those who make it.  In that regard, science really is self-correcting. If the data are available, then different analyses may give different results, but a consensus of the competent should emerge in the long run, leaving the valid conclusions stronger than before.

I'd welcome comments from those who have started to use open data and to hear your experiences, good or bad.

P.S. As I was finalising this post, I came across some great tweets from the OpenCon meeting taking place right now in Brussels. Anyone seeking inspiration and guidance for moving to an open science model should follow the #opencon hashtag, which links to materials such as these: Slides from keynote by Erin McKiernan, and resources at http://whyopenresearch.org/about.html.

The rationalist spa: an unmet need

I’ve had a few spa experiences, though I’m hardly a connoisseur. I've found  a spa is a good place to chill out and gossip with friends, and on the rare occasions when I stay at a fancy hotel, I’ve come to enjoy the process of whiling away the period between lunch and cocktails in a hot bubbly tub.

At the same time, I’ve become fascinated by the language used to advertise the available activities. I suspect most people who go to a spa don’t have any specific ailments, but they want to come away feeling more relaxed and vibrant, and the talk of 'therapies' and 'treatments' manages to create the comforting illusion that health can be shifted from suboptimal to optimal by various potions and practices. Particularly intriguing is the focus on foodstuffs. In a spa, you don’t ingest food: you rub it on the skin, sniff it, or slather yourself with it. I’ve always suspected there is an element of sublimation in this: most women who wish to remain slender have to suppress the desire to eat delicious things, and the spa provides an opportunity to interact with food without getting fat.

In the hotel I’ve been staying in you could be massaged with essential oils of grapefruit, have mango butter rubbed on your feet or head, be scrubbed with papaya and mandarin, or have your muscles relaxed by a concoction of rice and milk. Rather disappointingly, they didn't offer the ultimate decadence: a ‘chocolate wrap’, where you start with a warm milk soak, then get scrubbed with vanilla and bran, before being enveloped in a warm cocoa butter ‘masque’ (a word that always reminds me of Edgar Allan Poe's scary story).

It’s clear that there’s a lucrative market for this kind of thing. Many of us feel stressed by modern life, and if being smothered in chocolate or fruit makes us feel relaxed, why not?

Alas, though, for me the sense of relaxation is counteracted by irritation with the garbage that you have to endure while undergoing something as basic as a pedicure. Some of it is just overblown advertising guff, e.g. “Drawing on the elemental wisdom of nature, our treatments both invoke and restore the body’s natural equilibrium”. What does this even mean? The images are of blockage and decay being removed: “Clearing stagnant energy is the focus of the Spring Clean Scrub”. But the worst examples are those with medical overtones, with talk of healing, detoxification, and wellness. We are told that: “This wrap is highly effective in purging toxins and boosting the blood and lymphatic circulation” or "The polyphenols in cocoa delay the ageing process, causing you to look younger". Or even “The body is generously encased within a cooling serum”. Cripes! If you look up serum in a dictionary, this is a seriously scary idea.

I have, of course, always just gone with the flow. Attempting to debate the scientific basis of aromatherapy or ayurveda with a practitioner who makes their living administering these treatments is unlikely to make either of us more relaxed or vibrant. But I do wish someone would open a spa for rationalists, where one could go and get a good massage or get encased in mud just for the fun of it, without a lot of guff about energy blockages and deep-seated toxins.

Opportunity cost: A new red flag for evaluating interventions for neurodevelopmental disorders

Back in 2012, I wrote a blogpost offering advice to parents who were trying to navigate their way through the jungle of alternative interventions for children with dyslexia. I suggested a set of questions that should be asked of any new intervention, and identified a set of 'red flags', i.e., things that should make people think twice before embracing a new treatment.

The need for an update came to mind as I reflected on the Arrowsmith program, an educational approach that has been around in Canada since the 1980s, but has recently taken Australia and New Zealand by storm. Despite credulous press coverage in the UK, Arrowsmith has not, as far as I know, taken off here. Australia, however, is a different story, with Arrowsmith being taken up by the Catholic Education Office in Sydney after they found 'dramatic results' in a pilot evaluation.

For those who remember the Dore programme, this seems like an action replay. Dore was big in both the UK and Australia in the period around 2007-2008. Like Arrowsmith, it used the language of neuroscience, claiming that its approach treated the underlying brain problem, rather than the symptoms of conditions such as dyslexia and ADHD. Parents were clamouring for it, it was widely promoted in the media, and many people signed up for long-term payment plans to cover a course of treatment. People like me, who worked in the area of neurodevelopmental disorders, were unimpressed by the small amount of published data on the program, and found the theoretical account of brain changes unconvincing (see this critique). However, we were largely ignored until a Four Corners documentary was made by Australian ABC, featuring critics as well as advocates of Dore. Soon after, the company collapsed, leaving both employees of Dore and many families who had signed up to long-term financial deals, high and dry. It was a thoroughly dismal episode in the history of intervention for children with neurodevelopmental problems.

With Arrowsmith, we seem to be at the start of a similar cycle in Australia. Parents, hearing about the wondrous results of the program, are lobbying for it to be made more widely available. There are even stories of parents moving to Canada so that their child can reap the benefits of Arrowsmith. Yet Arrowsmith ticks many of the 'red flags' that I blogged about, lacks any scientific evidence for efficacy, and has attracted criticism from mainstream experts in children's learning difficulties. As with Dore, the Arrowsmith people seem to have learned that if you add some sciency-sounding neuroscience terms to justify what you do, people will be impressed. It is easy to give the impression that you are doing something much more remarkable than just training skills through repetition.

They also miss the point that, as Rabbitt (2015, p 235) noted regarding brain-training in general: "Many researchers have been frustrated to find that ability on any particular skill is surprisingly specific and often does not generalise even to other quite similar situations." There's little point in training children to type numbers into a computer rapidly if all that happens is that they get better at typing numbers into a computer. For this to be a viable educational strategy, you'd need to show that this skill had knock-on effects on other learning. That hasn't been done, and all the evidence from mainstream psychology suggests it would be unusual to see such transfer of training effects.

Having failed to get a reply to a request for more information from the Catholic Education Office in Sydney, I decided to look at the evidence for the program that was cited by Arrowsmith's proponents. An ongoing study by Dr Lara Boyd of the University of British Columbia features prominently on their website, but, alas, Dr Boyd was unresponsive to an email request for more information. It would seem that in the thirty-five years Arrowsmith has been around, there have been no properly conducted trials of its effectiveness, but there are a few reports of uncontrolled studies looking at children's cognitive scores and attainments before and after the intervention. One of the most comprehensive reviews is in the D.Phil. thesis of Debra Kemp-Koo from the University of Saskatchewan in 2013. In her introduction, Dr Kemp-Koo included an account of a study of children attending the private Arrowsmith school in Toronto:

All of the students in the study completed at least one year in the Arrowsmith program with most of them completing two years and some of them completing three years. At the end of the study many students had completed their Arrowsmith studies and left for other educational pursuits. The other students had not completed their Arrowsmith studies and continued at the Arrowsmith School. Most of the students who participated in the study were taking 6 forty minute modules of Arrowsmith programming a day with 1 forty minute period a day each of English and math at the Arrowsmith School. Some of the students took only Arrowsmith programming or took four modules of Arrowsmith programming with the other half of their day spent at the Arrowsmith school or another school in academic instruction (p. 34-35; my emphasis).

Two of my original red flags concerned financial costs, but I now realise it is important to consider opportunity costs: i.e., if you enlist your child in this intervention, what opportunities are they going to miss out as a consequence? For many of the interventions I've looked at, the time investment is not negligible, but Arrowsmith seems in a league of its own. The cost of spending one to three years working on unevidenced, repetitive exercises is to miss out on substantial parts of a regular academic curriculum. As Kemp-Koo (2013) remarked:

The Arrowsmith program itself does not focus on academic instruction, although some of these students did receive some academic instruction apart from their Arrowsmith programming. The length of time away from academic instruction could increase the amount of time needed to catch up with the academic instruction these students have missed. (p. 35; my emphasis).

References
Kemp-Koo, D. (2013). A case study of the Learning Disabilities Association of Saskatchewan (LDAS) Arrowsmith Program. Doctor of Philosophy thesis, University of Saskatchewan, Saskatoon.  

Rabbitt, P. M. A. (2015). The aging mind. London and New York: Routledge.

Publishing replication failures: some lessons from history

I recently travelled to Lismore, Ireland, to speak at the annual Robert Boyle summer school. I had been intrigued by the invitation, as it was clear this was not the usual kind of scientific meeting. The theme of Robert Boyle, who was born in Lismore Castle, was approached from very different angles, and those attending included historians of science, scientists, journalists, as well as interested members of the public. We were treated to reconstructions of some of Boyle's livelier experiments, heard wonderful Irish music, and we celebrated the installation of a plaque at Lismore Castle to honour Katherine Jones, Boyle's remarkable sister, who was also a scientist.

My talk was on the future of scientific scholarly publication, a topic that the Royal Society had explored in a series of meetings to celebrate the 350th Anniversary of the publication of Philosophical Transactions. I'm particularly interested in the extent to which current publishing culture discourages good science, and I concluded by proposing the kind of model that I recently blogged about, where the traditional science journal is no longer relevant to communicating science.

What I hadn't anticipated was the relevance of some of Boyle's writing to such contemporary themes.

Boyle, of course, didn't have to grapple with issues such as the Journal Impact Factor or Open Access payments. But some of the topics he covered are remarkably contemporary. He would have been interested in the views of Jason Mitchell, John L. Loeb Associate Professor of the Social Sciences at Harvard, who created a stir last year by writing a piece entitled "On the emptiness of failed replications". I see that the essay has now been removed from the Harvard website, but the main points can be found here*. It was initially thought to be a parody, but it seems to have been a sincere attempt at defending the thesis that "unsuccessful experiments have no meaningful scientific value." Furthermore, according to Mitchell, "Whether they mean to or not, authors and editors of failed replications are publicly impugning the scientific integrity of their colleagues." I have taken issue with this standpoint in an earlier blogpost; my view is that we should not assume that a failure to replicate a result is due to fraud or malpractice, but rather should encourage replication attempts as a means of establishing which results are reproducible.

I am most grateful to Eoin Gill of Calmast for pointing me to Robert Boyle's writings on this topic, and for sending me transcripts of the most relevant bits. Boyle has two essays on "the Unsuccessfulness of Experiments" in a collection of papers entitled “Certain Physiological Essays and other Tracts”. In these he discusses (at inordinate length!) the problems that arise when an experimental result fails to replicate. He starts by noting that such unsuccessful experiments are not uncommon:

… in the serious and effectual prosecution of Experimental Philosophy, I must add one discouragement more, which will perhaps as much surprize you as dishearten you; and it is, That besides that you will find …… many of the Experiments publish'd by Authors, or related to you by the persons you converse with, false or unsuccessful, … you will meet with several Observations and Experiments, which though communicated for true by Candid Authors or undistrusted Eye-witnesses, or perhaps recommended to you by your own experience, may upon further tryal disappoint your expectation, either not at all succeeding constantly, or at least varying much from what you expected. (opening passage)

He is interested in exploring the reasons for such failure; his first explanation seems equivalent to one that those using statistical analyses are all too familiar with – a chance false positive result.

And that if you should have the luck to make an Experiment once, without being able to perform the same thing again, you might be apt to look upon such disappointments as the effects of an unfriendliness in Nature or Fortune to your particular attempts, as proceed but from a secret contingency incident to some experiments, by whomsoever they be tryed. (p. 44)

And he urges the reader not to be discouraged – replication failures happen to everyone!

…. though some of your Experiments should not always prove constant, you have divers Partners in that infelicity, who have not been discouraged by it. (p. 44)

He identifies various possible systematic reasons for such failure: a problem with skill of the experimenter, with purity of ingredients, or variation in the specific context in which the experiment is conducted. He even, implicitly, addresses statistical power, noting how one needs many observations to distinguish what is general from individual variation.

…the great variety in the number, magnitude, position, figure, &c. of the parts taken notice of by Anatomical Writers in their dissections of that one Subject the humane body, about which many errors would have been delivered by Anatomists, if the frequency of dissections had not enabled them to discern betwixt those things that are generally and uniformly found in dissected bodies, and those which are but rarely, and (if I may so speak) through some wantonness or other deviation of Nature, to be met with. (p. 94)

Because of such uncertainties, Boyle emphasises the need for replication, and the dangers of building complex theory on the basis of a single experiment:

….try those Experiments very carefully, and more than once, upon which you mean to build considerable Superstructures either theorical or practical, and to think it unsafe to rely too much upon single Experiments, especially when you have to deal in Minerals: for many to their ruine have found, that what they at first look'd upon as a happy Mineral Experiment has prov'd in the issue the most unfortunate they ever made. (p. 106)

I'm sure there are some modern scientists who must be thinking their lives may have been made much easier if they had heeded this advice. But perhaps the most relevant to the modern world, where there is such concern about the consequences of failure to replicate, are Boyle's comments on the reputational impact of publishing irreproducible results:

…if an Author that is wont to deliver things upon his own knowledge, and shews himself careful not to be deceived, and unwilling to deceive his Readers, shall deliver any thing as having try'd or seen it, which yet agrees not with our tryals of it; I think it but a piece of Equity, becoming both a Christian and a Philosopher, to think (unless we have some manifest reason to the contrary) that he set down his Experiment or Observation as he made it, though for some latent reason it does not constantly hold; and that therefore though his Experiment be not to be rely'd upon, yet his sincerity is not to be rejected. Nay, if the Author be such an one as has intentionally and really deserved well of Mankind, for my part I can be so grateful to him, as not only to forbear to distrust his Veracity, as if he had not done or seen what he says he did or saw, but to forbear to reject his Experiments, till I have tryed whether or no by some change of Circumstances they may not be brought to succeed. (p. 107)

The importance of fostering a 'no blame' culture was one theme that emerged in a recent meeting on Reproducibility and Reliability of Biomedical Research at the Academy of Medical Sciences. It seems that in this, as in so many other aspects of science, Boyle's views are well-suited to the 21st century.

For more on Robert Boyle, see here


12th July 2015: Thanks to Daniël Lakens who pointed me to the Wayback machine, where earlier versions of the article can be found:   http://web.archive.org/web/*/http://wjh.harvard.edu/~jmitchel/writing/failed_science.htm

How the media spun the Tim Hunt story

 I had vowed not to blog about the Tim Hunt affair. I thought everything that could have been said had been said, and I'd made my own position clear in a comment on Athene Donald's blog, and in a comment in the Independent.

But then I came across Stephen Ballentyne's petition to "Bring Back Tim Hunt", and I was transported back five years to my first ever blog post on "Academic Mobbing in Cyberspace," a strange tale about sex, fruitbats and internet twittermobs. I started blogging in 2010 because I wanted to highlight how the internet encourages people to jump in to support causes without really examining the facts of the matter. The Ballentyne petition points to an uncannily similar conclusion.

Let me start out by saying I am not arguing against people's right to take Tim Hunt's side. As many people have noted, he is a well-liked man who has done amazing science and there are many women as well as men who will speak up for him as a supporter of female scientists. Many of those who support him do so in full knowledge of the facts, out of a sense of fairness and, in the case of those who know him personally, loyalty.

My concern is about the number of signatories of Ballentyne's petition who have got themselves worked up into a state of indignation on the basis of wrong information. There are three themes that run through the comments that many people have posted:

a) They think that Tim Hunt has been sacked from his job

b) They think he is 'lost to science'

c) They think University College London (UCL) fired him in response to a 'Twitter mob'.

None of these things is true. (a) Hunt is a retired scientist who was asked to resign from an honorary position.  That's shaming and unpleasant, but an order of magnitude different from being sacked and losing your source of income. (b) Hunt continues to have an affiliation to the Crick Institute – a flagship research centre that recently opened in Central London. (c) UCL are explicit that their acceptance of his resignation from an honorary position had nothing to do with the reaction on social media.

So why do people think these things? Quite simply, this is the interpretation that has been put about in many of the mainstream media. The BBC has been particularly culpable. The Today programme on Radio 4 ran a piece which started by saying Hunt had 'lost his job'. This was a couple of days after the UCL resignation, when any self-respecting journalist would have known this to be false. Many newspapers fuelled the flames. An interview with Boris Johnson on the BBC website added the fictitious detail that Hunt had been sacked by the Royal Society. He is in fact still a Fellow – he has simply been asked to step down from a Royal Society committee. It is interesting to ask why the media are so keen to promote the notion of Hunt as victim, cruelly dismissed by a politically correct university.

It's fascinating analysing the comments on the petition.  After deleting duplicates, there were 630 comments. Of those commenters where gender could be judged, 71% were male. Rather surprisingly, only 52% of commenters were from the UK, and 12% from the US, with the remainder scattered all over the world.

There were 93 comments that explicitly indicated they thought that Hunt had been sacked from his job, and/or was now 'lost to science' – and many more that called for his 'reinstatement', where it was unclear whether they were aware this was an honorary position.  They seemed to think that Hunt was dependent on UCL for his laboratory work, and that he had a teaching position. For instance, "Don't let the world lose a great scientist and teacher over a stupid joke." I would agree with them that if he had been sacked from a regular job, then UCL's action would have been disproportionate. However, he wasn't.

Various commentators drew comparisons with repressive fascist or Marxist states, e.g. "It is reminiscent of the cultural revolution in China where 'revisionist' professors were driven out of their offices by their prospective students, to do farm labour." And there was an awful lot of blaming of women, Twitter and feminism in general, with comments such as "Too much of this feminist ranting going on. Men need to get their spines back and bat it away" and "A respected and competent scientist has been hounded out of his job because of an ignorant baying twitter mob who don't happen to like his views". And my favourite: "What he said was a joke. If lesbian feminist women can't take a joke, then they are the joke." Hmm.

It's unfortunate that the spread of misinformation about Hunt's circumstances have muddied the waters in this discussion.  A minority of those commenting on Ballentyne's petition are genuine Hunt supporters who are informed of the circumstances; the bulk seem to be people who are concerned because they have believed the misinformation about what happened to Hunt; a further set are opportunistic misogynists who do Hunt no favours by using his story as a vehicle to support their dislike of women. There is a much more informed debate in the comments section on Athene Donald's blog, which I would recommend to anyone who wants to understand both sides of the story.

My collapse of confidence in Frontiers journals

Frontiers journals have become a conspicuous presence in academic publishing since they started in 2007 with the advent of Frontiers in Neuroscience. When they were first launched, I, like many people, was suspicious. This was an Open Access (OA) online journal where authors paid to publish, raising questions about the academic rigour of the process. However, it was clear that the publishers had a number of innovative ideas that were attractive to authors, with a nice online interface and a collaborative review process that made engagement with reviewers more of a discussion than a battle with anonymous critics. Like many other online OA journals, the editorial decision to publish was based purely on an objective appraisal of the soundness of the study, not on a subjective evaluation of importance, novelty or interest. As word got round that respectable scientists were acting as editors, reviewers and authors of paper in Frontiers, people started to view it as a good way of achieving fast and relatively painless publication, with all the benefits of having the work openly available and accessible to all.

The publishing model has been highly successful. In 2007, there were 45 papers published in Frontiers in Neuroscience, whereas in 2014 it was 3,012 (data from Scopus search for source title Frontiers in Neuroscience, which includes Frontiers journals in Human Neuroscience, Cellular Neuroscience, Molecular Neuroscience, Behavioral Neuroscience, Systems Neuroscience, Integrative Neuroscience, Synaptic Neuroscience, Aging Neuroscience, Evolutionary Neuroscience and Computational Neuroscience). If all papers attracted the author fee of US$1900 (£1243) for a regular article, this would bring in £3.7 million pounds in 2014: the actual income would be less than this because some articles are cheaper, but it's clear that the income is any in case substantial, especially since the journal is online and there are no print costs. But this is just the tip of the iceberg. Frontiers has expanded massively since 2007 to include a wide range of disciplines.  A Scopus search for articles with journal title that includes "Frontiers in" found over 54,000 articles since 2006, with 10,555 published in 2014.

With success, however, have come growing rumbles of discontent. Questions are being raised about the quality of editing and reviewing in Frontiers.  My first inkling of this was a colleague told me he would not review for Frontiers because his name was published with the article. This wasn't because he wanted confidentiality; rather he was concerned that it would appear he had given approval for the article, when in fact he had major reservations.

Then, there have been some very public criticisms of editorial practices at Frontiers. The first was associated with the retraction of a paper that claimed climate denialism was associated with a more general tendency to advocate conspiracy theories. Papers on this subject are always controversial and this one was no exception, attracting complaints to the editor. The overall impression from the account in Retraction Watch was that the editor caved in to legal threats, thereby letting critics of climate change muzzle academic freedom of speech. This led to the resignation of one Frontiers editor**.

Next, there was a case that posed the opposite problem: the scientific establishment were outraged that a paper on HIV denial had been published, and argued that it should be retracted. The journal editor decided that the paper should not be retracted, but instead rebranded it as Opinion – see Retraction Watch account here.

Most recently, in May 2015 there was a massive upset when editors of the journals Frontiers in Medicine and Frontiers in Cardiovascular Medicine mounted a protest at the way the publisher was bypassing their editorial oversight and allocating papers to associate editors who could accept them without the knowledge of the editor in chief. The editors protested and published a manifesto of editorial independence, leading to 31 of them being sacked by the publisher.   

All of these events have chipped away at my confidence in Frontiers journals, but it was finally exploded completely when someone on Twitter pointed me to this article entitled "First time description of dismantling phenomenon" by Laurence Barrer and Guy Giminez from Aix Marseille Université, France. I had not realised that Frontiers in Psychology had a subsection on Psychoanalysis and Neuropsychoanalysis, but indeed it does, and here was a paper proposing a psychoanalytic account of autism. The abstract states: "The authors of this paper want to demonstrate that dismantling is the main defense mechanism in autism, bringing about de-consensus of senses." Although the authors claim to be adopting a scientific method for testing a hypothesis, it is unclear what would constitute disproof. Their evidence consists of interpreting known autistic characteristics, such as fascination with light, in psychoanalytic terms. The source of dismantling is attributed to the death drive. This reads like the worst kind of pseudoscience, with fancy terminology and concepts being used to provide evidence for a point of view which is more like a religious belief than a testable idea. I wondered who was responsible for accepting this paper.  The Editor was Valeria Vianello Dri, Head of Child and Adolescent Neuropsychiatry Units in Trento, Italy. No information on her biography is provided on the Frontiers website. She lists four publications: these are all on autism genetics. All are multi-authored and she is not first or last author on any of these*. A Google search confirmed she has an interest in psychoanalysis but I could find no further information to indicate that she had any real experience of publishing scientific papers. There were three reviewers: the first two had no publications listed on their Frontiers profiles; the third had a private profile, but a Google search on his name turned up a CV but it did not include any peer-reviewed publications.

So it seems that Frontiers has opened the door to a branch of pseudoscience to set up its own little circle of editors, reviewers and authors, who can play at publishing peer-reviewed science. I'm not saying all people with an interest in psychoanalysis should be banished: if they do proper science, they can publish that in regular journals without needing this kind of specialist outlet. But this section of Frontiers is a disastrous development; there is no evidence of scientific rigour, yet the journal gives credibility to a pernicious movement that is particularly strong in France and Argentina, which regards psychoanalysis as the preferred treatment for autism. Many experts have pointed out that this approach is not evidence-based, but worse still, in some of its manifestations it amounts to maltreatment.  What next, one wonders? Frontiers in homeopathy?

Like the protesting editors of Frontiers in Medicine, I think the combined evidence is that Frontiers has allowed the profit motive to dominate. They should be warned, however, that once they lose a reputation for publishing decent science, they are doomed. I've already heard it said that someone on a grants review panel commented that a candidate's articles in Frontiers should be disregarded. Unless these journals can recover a reputation for solid science with proper editing and peer review, they will find themselves shunned.

*The Frontiers biography suggests she is last author on a paper in 2008, but the author list proved to be incomplete.
** Correction: Shortly after I posted this, Stephan Lewandowsky wrote to say that there were 3 editors who resigned over the RF retraction, plus another one voicing intense criticism