A response to a wayward defence of a concerted critique of a bad argument about science and religion

And breathe. 

Ananyo Bhattacharya, chief online Editor of Nature Magazine, has penned a strident defence of this remarkable piece by Daniel Sarewitz on science and religion. In his response, Bhattacharya takes issue with my critique of Sarewitz's arguments, which you can read here.

I've responded to Ananyo, but the moderators at Discover magazine don't seem to work weekends (fair enough) so I've copied below my response.

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As the “one critic” that Ananyo cites, I guess I ought to respond. I have a lot of respect for Ananyo, but his post strikes me as a muddled mix of non sequiturs and rapidly shifting goal posts.

First, the example of MRI is a straw man. I argued that the scientific method is the best way of understanding reality but this in no way reduces the mode of that understanding to any one form of investigation. I could just as easily adopt a scientific method to explore the psychology and phenomenology of a person’s response to the Dark Knight and, in doing so, learn a great deal about emotion and cognition. Unless, that is, Ananyo is arguing that psychology isn’t a real science, or that studying the brain is the only way to understand mental processes (I sincerely hope he isn’t).

To give Ananyo the benefit of the doubt, perhaps he is instead referring to the hard problem of consciousness, that no amount of scientific enquiry can ever fully illuminate the subjective experience of another person. In other words, could I ever know whether your experience of the Dark Knight is the same as mine? Some philosophers, like Dennett, have argued that the hard problem is itself an illusion, but even if it is a genuine question then the answer may lie behind a technological barrier rather than a philosophical one. Unless there is a ghost in the machine, or a supernatural world beyond our ability to study, anything that can be ‘experienced’ can conceivably be measured and studied in a scientific manner.

Second, Ananyo argues that because I believe the scientific method is the best way of understanding reality that me and other critics are “bash[ing] those that dare to suggest that one might experience wonder and awe”, and “dismiss[ing] culture without a second thought”. 

This is another straw man, and a mildly offensive one at that. My point in responding to Sarewtiz was simply that such feelings of awe and wonder – such us religious experiences – tell us nothing about reality. End of. A scientific study of wonder and awe itself could tell us about the basis of those emotions, but simply experiencing something is not the same thing as studying it or understanding it. I would argue that to understand something requires us to interpret our experiences through a rational filter.

Third, in my critique of Sarewitz I said that science is not just the best way of understanding reality, but the “best and only”. I agree that the use of “only” here is debatable, and whether others agree or not may depend on their definition of what science is. There is no real consensus on the necessary and sufficient conditions for something to be “scientific” but my view is quite open, which is to say that science – in it’s most basic form – is simply a way of appraising evidence through logic. The way in which this methodology is applied, and the stringency, varies across academic disciplines. But the scientific method is by no means the purview of the traditional sciences; many disciplines in the humanities (e.g. history) adopt what I would regard as a form of the scientific method, and historians I know agree.

For anyone interested, Neuroskeptic’s post on ‘what is science’ is well worth reading.

Fourth, Ananyo equates the criticism of Sarewitz with logical positivism. I’ll happily admit my knowledge of philosophy isn’t great, but my understanding is that the arguments by me and others are equally consistent with postpositivism. And if not, why not?

Finally, it’s disappointing to see the pejorative “scientistas”, as though the critiques of Sarewitz are necessarily an argument for scientism (yet another straw man, sigh). Perhaps Ananyo means this in a tongue-in-cheek way, but reading it as written it does come across as an insult to many readers of Nature magazine. Good luck with that one mate!

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The Dirty Dozen: A wish list for psychology and cognitive neuroscience

It’s been quite a month in science. 

On the bright side, we probably discovered the Higgs boson (or at least something that smells pretty Higgsy), and in the last few days the UK Government and EU Commission have made a strong commitment to supporting open-access publishing. In two years, so they say, all published science in Britain will be freely available to the public rather than being trapped behind corporate paywalls. This is a tremendous move and I applaud David Willetts for his political courage and long-term vision.

On the not-so-bright side, we’ve seen a flurry of academic fraud cases. Barely a day seems to pass without yet another researcher caught spinning yarns that, on reflection, did sound pretty far-fetched in the first place. What’s that? Riding up rather than down an escalator makes you more charitable? Dirty bus stops make you more racist? Academic fraudsters are more likely to have ground-floor offices? Ok, I made that last one up (or rather, Neuroskeptic did) but if such findings sound like bullshit to you, well funnily enough they actually are. Who says science isn’t self-correcting?

We owe a great debt to Uri Simonsohn, the one-man internal affairs bureau, for judiciously uncovering at least three cases of fraudulent practice in psychological research. So far his investigations have led to two resignations and counting. Bravo. This is a thankless task that will win him few friends, and for that alone I admire him.

And as if to remind us that fraud is by no means unique to psychology, enter the towering Godzilla of mega-fraud – Japanese anaesthesiologist, Yoshitaka Fujii, who has achieved notoriety by becoming the most fraudulently productive scientist ever known.

(As an aside, has anyone ever noticed how the big frauds in science always seem to be perpetrated by men? Are women more honest or do they just make savvier fraudsters?)

Along with all the talk of fraud in psychology, we have had to tolerate the usual line-up of  ‘psychology isn’t science’ rants from those who ought to learn something before setting hoof to keyboard. Fortunately we have Dave Nussbaum to sort these guys out, which he does with a steady hand and a sharp blade. Thank you, Dave!

With psychological science facing challenges and shake-ups on so many different fronts, the time seems ripe for some self-reflection. I used to believe we had a firm grasp on methodology and best practice. Lately I’ve come to think otherwise.

So here’s a dirty dozen of suggested fixes for psychology and cognitive neuroscience research that I’ve been mulling over for some time. I want to stress that I deserve no credit for these ideas, which have all been proposed by others.

1.     Mandatory inclusion of raw data with manuscript submissions

No ifs. No buts. No hiding behind the lack of ethics approval, which can be readily obtained, or the vagaries of the Data Protection Act. Everyone knows data can be anonymised.

2.     Random data inspections

We should conduct fraud checks on a random fraction of submitted data, perhaps using the methodology developed by Uri Simonsohn (once it is peer reviewed and judged statistically sound – as I write this, the technique hasn’t yet been published). Any objective test for fraud must have a very low false discovery rate because the very worst thing would be for an innocent scientist to be wrongly indicted. Fraudsters tend to repeat their behaviour, so the likelihood of false positives in multiple independent data sets from the same researcher should (hopefully) be infinitesimally small.

3.     Registration of research methodology prior to publication

Some time ago, Neuroskeptic proposed that all publishable research should be pre-registered prior to being conducted. That way, we would at least know from the absence of published studies how big the file-drawer is. My first thoughts on reading this were: why wouldn’t researchers just game the system, “pre” registering their research after the experiments are conducted? And what about off-the-cuff experiments conjured up over a beer in the pub?

As Neuroskeptic points out, the first problem could be solved by introducing a minimum 6-month delay between pre-registration and data submission. Also, all prospective co-authors of a pre-registration submission would need to co-sign a letter stating that the research has not yet been conducted.

The second problem is more complicated, but also tractable. My favourite solution is one posed by Jon Brock. Empirical publications could be divided into two categories, Experiments and Observations.  Experiments would be the gold standard of hypothesis-driven research. They would be pre-registered with methods (including sample size) and proposed analyses pre-reviewed and unchangeable without further re-review. Observations would be publishable but have a lower weight. They could be submitted without pre-registration, and to protect against false positives, each experiment from which a conclusion is drawn would be required to include a direct internal replication.

4.     Greater emphasis on replication

It’s a tired cliché, but if we built aircraft the way we do psychological research, every new plane would start life exciting and interesting before ending in an equally exciting fireball. Replication in psychology is dismally undervalued, and I can’t really figure out why this is when everyone, even journal editors, admit how crucial it is. It’s as though we’re trapped in some kind of groupthink and can’t get out. One solution, proposed by Nosek, Spies and Motyl, is the development of a metric called the Replication Value (RV). The RV would tell us which effects are most worth replicating. To quote directly from their paper, which I highly recommend:

Metrics to identify what is worth replicating. Even if valuation of replication increased, it is not feasible – or advisable – to replicate everything. The resources required would undermine innovation. A solution to this is to develop metrics for identifying Replication Value (RV)– what effects are more worthwhile to replicate than others? The Open Science Collaboration (2012b) is developing an RV metric based on the citation impact of a finding and the precision of the existing evidence of the effect. It is more important to replicate findings with a high RV because they are becoming highly influential and yet their truth value is still not precisely determined. Other metrics might be developed as well. Such metrics could provide guidance to researchers for research priorities, to reviewers for gauging the “importance” of the replication attempt, and to editors who could, for example, establish an RV threshold that their journal would consider as sufficiently important to publish in its pages.

I think this is a great idea. As part of the manuscript reviewing process, reviewers could assign an RV to specific experiments. Then, on a rolling basis, the accepted studies that are assigned the highest weightings would be collated and announced. Journals could have special issues focusing on replication of leading findings, with specific labs invited to perform direct replications and the results published regardless of the outcome. This method could also bring in adversarial collaborations, in which labs with opposing agendas work together in an attempt to reproduce each other’s results.

5.     Standardise acceptable analysis practices

Neuroimaging analyses have too many moving parts, and it is easy to delude ourselves that the approach which ends up ‘working’ (after countless reanalyses) is the one we originally intended. Psychological analyses have fewer degrees of freedom but this is still a major problem. We need to formulate a consensus view on gold standard practices for excluding outliers, testing and reporting covariates, and inferential approaches in different situations. Where multiple legitimate options exist, supplementary information should include analyses of them all, and raw data should be available to readers (see point 1).

6.     Institute standard practices for data peeking

Data peeking isn't necessarily bad, but if we do it then we need to correct for it. Uncorrected peeking runs riot in psychology and neuroimaging because the pressure to publish and the dependence of publication on significant results has made chasing p-values the norm. We can see it in other areas of science too. Take the Higgs. Following initial hints at 3-sigma last year, the physicists kept adding data until they reached 5-sigma. The fact that their alpha is so stringent in the first place provides reassurance that they have genuinely discovered something. But if they peeked and chased then it simply isn’t the 5-sigma discovery that was advertised. (As a side note: how about we ditch Fisher-based stats altogether and go Bayesian? That way we can actually test that pesky null hypothesis)

7.     Officially recognise quality of publications over quantity

Everyone agrees that quality of publications is paramount, but we still chase quantity and value ‘prolific’ researchers. So how about setting a cap on the number of publications each researcher or lab can publish per year? That way we would truly have an incentive to make sure of results before publishing them. It would also encourage us to publish single papers with multiple experiments and more definitive conclusions.

8.     Ditch impact factor and let us never speak of it again

As scientists who purportedly know something about numbers, we should be collectively ashamed of ourselves for being conned by journal impact factors (IF). Nowhere is the ludicrous doublethink of the IF culture more apparent than in the current REF, where the advice from universities amounts to “IF of journals is not taken into account in assessing quality of your REF submissions” while simultaneously advising us to “ensure that your four submissions are from the highest impact journals”. Complete with helpful departmental emails reminding us which journals are going up in IF (which is all of them as far as I can tell), the situation really is quite stupid and embarrassing. Here’s a fact shown by Bjorn Brembs: IF correlates better with retraction rate than citation rate. We should replace IF with article-specific merits such as post-publication ratings, article citation count, or – shock horror – considered assessment of the article after reading the damn thing.

9. Open access publication

Much has been said and written in the last few days about open access, with the Government making important steps toward an open scientific future in the UK (I recommend following the blogs of Stephen Curry and Mike Taylor for the latest developments and analysis).  For my part, I think the sooner we eliminate corporate publishers the better. I simply don’t see what value they add when all of the reviewing and editing is done by us at zero cost.

10. Stop conflating research inputs with research outputs

Getting a research grant is great, but we need to stop counting grants as outputs. They are inputs. We need to start assessing the quality of science by balancing outputs against inputs, not by adding them together.

11. Rethink authorship

Academic authorship is antiquated and not designed for collaborative teams. By rank-ordering authors from first to last, we make it impossible for multiple co-authors to make a genuinely equal contribution (Ah, I hear you cry, what about that little asterisk that flags equal contributions? Well, sorry, but…um…nobody really takes much notice of those).

I think a better approach would be to list authors alphabetically on all papers and simply assign % contributions to different areas, such as experimental design, analysis, data collection, interpretation of results, and manuscript preparation. Some journals already do this in some form, but I would like to see this completely replace the current form of authorship.

12. Revise the peer review system

Independent peer review may the best mechanism we currently have for triaging science, but it still sucks. For one thing, it’s usually not independent. I often get asked to review papers by scientists I know or have even worked with. I’ve even been asked to review my own papers on occasion, and was once asked to review my own grant application! (You’ll be glad to know I declined all such instances of self-review). The review process is random and noisy, and based on such a pitifully small sample of comments that the notion of it providing meaningful information is, statistically speaking, quite ridiculous. 

I personally favour the idea of cutting down on the number of detailed reviewers per manuscript and instead calling on a larger number of ‘speed reviewers’, who would simply rate the paper according to various criteria, without having to write any comments. As a reviewer, I often find that I can form an opinion of an article relatively quickly – it is writing the review that takes the most time.

Last week, Paul Knoepfler wrote a provocative blog post proposing an innovation in peer review in which authors review the reviewers. Could this help improve quality of reviews? Unfortunately, I don’t think Paul’s system would work (see my comment on his post here), but perhaps some kind of independent meta-review of reviewers could also be a good idea in a limited number of cases. 

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What do you think? Got better ideas? Please leave any comments below. 

** Update 18/7/12, 14:30: On the issue of the gender imbalance in academic fraud, Mark Baxter has kindly reminded me of this case involving Karen M. Ruggiero. 

Research Briefing: Can boosting motor inhibition help us resist temptation?

A lot of enjoyable things in life are risky and potentially addictive. So how do we control our impulses? And why do some people find it harder to say ‘no’ than others?

In a recent study we asked whether a key to self-control could lie in an unexpected place: a corner of our cognitive system that controls motor actions. We found that when people did a simple task that required starting and stopping finger movements, they also took less risk when gambling. This effect lasted at least two hours after being trained in so-called ‘motor inhibition’.

Why should the act of inhibiting simple movements lead to more cautious gambling behaviour? We don't yet know, but our working hypothesis is that it boosts or primes an inhibition system in the brain that regulates a range of functions - including complex decision-making. By strengthening motor inhibition through the mental equivalent of a ‘gym workout’ we may be able to open new avenues for treating problem gambling and other addictions.

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Source article: Verbruggen, F., Adams, R., & Chambers, C.D. (2012). Proactive motor control reduces monetary risk taking in gambling. Psychological Science, 23, 805-815. [pdf] [press release]

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Imagine the following scenario. You are driving to meet your financial adviser for a meeting about your investments. Along the way you encounter a series of obstacles that cause you to drive with extra caution: roadworks, speed cameras, and intermittent bursts of rain. When you eventually arrive and sit down with your adviser, she asks how you would like to spread your reserves between a number of low- and high-risk options. Choosing isn’t easy – the higher risk investments could pay for that much-needed vacation in the Maldives, but the market is unpredictable and you could lose out. You make your choices.

Clearly this decision is complex and based on many different sources of information. But ask yourself: would your decision have been the same if the journey to the meeting had been free of obstacles? Intuitively, you’re probably thinking “Huh? I would select my investments rationally, why should the drive there make any difference?” And most people would agree with you – society reinforces the notion that being able to make decisions rationally and without bias is part of what ‘makes us human’.

There’s just one problem with this argument: it doesn’t quite fit the evidence. Previous research tells us that multitasking impairs cognition, and we also know that priming people in various ways can bias social attitudes and financial decisions that we would intuitively ascribe to our free will. A recent study, for example, found that priming people with the mere image of a thinking man reduced their religious beliefs. At the same time, taxing self-control can cause what social psychologists call ego depletion, reducing our ability to resist temptation.

So, are you still sure that your cautious driving would have no effect on your investment decisions?

Spreading caution around

If our ability to make rational decisions can be influenced by cognitive interference, then you might assume that such effects should impair decision-making. Some evidence does indeed suggest that taxing executive control can make it harder for people to inhibit impulsive choices, although not all studies agree.

But what if we could specifically tailor a kind of multitasking that would improve your decision-making? In other words, what if the interference somehow biased you to take less risk, like the example above with cautious driving? To test this idea, we designed a laboratory task that brings together two different forms of decision-making: monetary gambling and basic stopping of a motor response.

Here’s how it worked. On each trial of the task, people were presented with six options below a series of yellow bars. Each of these options was a number of points that could be won, which – depending on the condition – ranged from 2 to 448. Higher amounts were intuitively more attractive but, crucially, also had a lower chance of winning. And if you did lose the gamble then you forfeited half the amount wagered. So, for instance, if you picked ‘112’ you had only a 15% chance of winning the 112 points, but an 85% chance of losing 66 points. Whereas if you picked ‘2’ you had a 75% chance of winning those 2 points, and only a 25% change of losing 1 point.

We didn’t tell people the exact probabilities of winning or losing, but we did tell them that the chances of winning were lower for higher amounts. We then calculated a simple betting score by taking the average of the choices across the options: from 1 to 6, ranked in order of lowest risk to highest risk. This means that the higher the score, the more willing the participant was to take risks when gambling. At the end of the experiment participants were paid the overall amount they won, at a rate of 1000 points to £1.

On each trial of this task, participants were given a few seconds to reach a decision before the yellow bars started rising toward a white line. Once the bars reached the line they then pressed whichever key corresponded to their choice. This was followed by feedback as to how many points they won or lost on that trial, plus a readout of their overall points balance.

Our behavioural task for combining monetary gambling with motor inhibition. The upper panel (A) shows a typical sequence of stimuli on trials without motor inhibition (called  ‘no-signal’ trials). The first screen (left) presented the various possible choices, ranging from smaller low-risk amounts, to great high-risk amounts. The letters below each option reminded participants which key on the keyboard corresponded to which choice. After 3.5 seconds the bars began to rise and participants made their response when the bars reached the white line. They then received feedback indicating whether their wager was successful or not, and their overall points balance. The lower panel (B) shows a sequence of stimuli on a trial that involved motor inhibition (‘signal’ trials). Everything is the same as (A), except that the bars now turn black just before reaching the white line.

To test how stopping of simple responses (i.e. motor inhibition) interacts with gambling decisions, we introduced an additional catch. Sometimes the bars would turn black just before reaching the white line. On these trials, participants were told to stop whatever decision they had planned. If they stopped successfully then they would win points, but if they failed to stop they would lose points.

The critical manipulation in this experiment was the expectation of stopping. To achieve this we further split the task into blocks of trials in which participants either expected ‘stop signals’ to occasionally occur (dual-task blocks, so named because these blocks included two tasks, gambling and stopping) or in which they were told in advance that signals would never occur (single-task blocks, so named because these blocks only included the gambling task).

We then compared the average betting scores between the blocks, focusing specifically on the trials without stop-signals. This allowed us to directly compare the effect on gambling of either expecting or not expecting to stop a response, while keeping everything else the same. In other words, the only thing that differed between these two conditions was the participant’s cognitive expectations.

So what did we predict would happen? There are two main possibilities. On the one hand, when people were in dual-task blocks they were now dividing their attention between two tasks. It is possible that this state of divided attention and cognitive ‘load’ could interfere with decision-making in the gambling task, making it harder for people to resist the more tempting, higher-risk options. We called this hypothesis the interference account.

On the other hand, we also know that when people expect to stop a response they become more cautious in their motor control – mainly, they slow down. So could this state of motor cautiousness transfer or spread to other forms of decision-making? If so, then when people expect to stop their response in the dual-task blocks, they might actually become more cautious and so take less risk than in the single-task blocks. We called this hypothesis the transfer account.

So which hypothesis won in the contest between interference and transfer? The results clearly supported the transfer account. When people expected to stop their motor response, their betting score decreased by 10-15% compared with when they knew they wouldn’t have to stop. So when people were expecting that they might have to stop their response, they freely chose to place less risky bets.

To be sure that this effect was specific to motor inhibition, rather than attention or other general effects of cognitive load, we also tested another group of participants in a ‘double-response’ control condition. Rather than stopping their response on signal trials, participants in the double-response group made an extra response. The double-response group showed no such reduction in risky gambling (in fact, it increased slightly), which helps tie the effects in the stop group to inhibition. And to be sure that these findings weren’t a statistical fluke, we ran the whole experiment twice in different participants to replicate the main finding.

The results of our first experiment. The left figure (A) plots the average betting score in the two groups of participants (double-response vs. stop) and for the two different conditions (single task vs. dual task). A higher betting score indicates riskier betting behaviour. Notice how the betting score is reduced under dual task vs. single task conditions in the stop group only (arrow; red bar). The right figure (B) shows the distribution of choices in the stop group, from the lowest risk (1) to the highest risk (6). Notice how expecting to stop a response  in the dual-task condition increased the proportion of lowest-risk responses (arrow) compared to blocks where participants never expected to stop (single task condition).

What do these results signify? From a theoretical perspective they reveal an overlap between different forms of inhibition: inhibition of motor responses causally shaped inhibition of risky gambling decisions. Previous studies have hinted at that such links might exist but much of this evidence relies on correlation rather than causation. For instance, people with a gambling addiction can sometimes show impairments in motor inhibition but it is unclear whether these problems are causally related.

Having uncovered evidence for a causal link we next asked whether training people in motor inhibition could have a more lasting effect. If so, this would suggest that the relationship between motor inhibition and risk-taking behaviour might be developed as a complementary therapy for addiction.

Bootcamp for inhibition?

In the next series of experiments we asked whether training people to stop responses could reduce risk-taking later in time. The idea was to train people for a short period (about 30 minutes) at motor inhibition, followed by monetary gambling. The gambling task was the same as described above but including the single-task blocks only, i.e. the bars never turned black and participants never expected to stop their responses while gambling.

We began by dividing people into three training groups. The stop group did a standard motor inhibition task, called the stop-signal task. The double-response group did a different (non-inhibition) task on the same stimuli. The control group didn’t do any training – they just skipped straight to the gambling task.

The stop-signal task is a workhorse of experimental psychology made famous by Gordon Logan, and one of the most straightforward and elegant tests of cognitive function. In our version of the task, participants were shown a shape on a computer screen (square or diamond) and were asked to identify the shape as quickly as possible by pressing one of two buttons, e.g. left button for a square vs. right button for a diamond.

On a random third of trials, the shape turned bold after a short delay. These trials are called ‘signal trials’ and the participant is instructed to try and stop their response. Successfully stopping your response is easy when the signal occurs immediately after the shape appears, but it becomes progressively more difficult as the delay between shape and the stop-signal is increased. This is because, at longer delays, you will be closer to executing your initial response by the time the signal occurs, so there is less time to countermand that response.

Our double-response group did a control task on the same stimuli: instead of trying to stop their response on signal trials, they instead executed a second response. So their task had similar attentional demands as the stop-signal task, but crucially without requiring motor inhibition.

The training phase in our second series of experiments. On ‘no-signal’ trials, participants decided as quickly as possible whether the stimulus was a square or a diamond. On a third of trials, the shape turned bold after a variable delay, termed a stimulus onset asynchrony (SOA). How participants responded on these ‘signal’ trials depended on which group they were in. Those in the stop group attempted to cancel their original response, while those in the double-response group made a second response. The numbers in the figure indicate the duration of the different events, in milliseconds.

So what might happen if we give participants the stop-signal task followed by the gambling task? If the effect of motor inhibition transfers over time to risk-taking behaviour then we expected training to make people more cautious in their gambling decisions, producing a similar effect to the first series of experiments. On the other hand, requiring people to continuously start and stop for 30 minutes might fatigue their inhibitory control and lead to increased risk-taking.

Once again the results were clear: motor inhibition training reduced risky gambling by 10-15%. Interestingly, we saw the same pattern even when we introduced a 2-hour gap between the end of the stop training and the start of the gambling task.

Training in motor inhibition reduced risk-taking in the gambling task by 10-15%. Note how the red bars are lowest when the gambling task immediately followed training (left set of bars), even after a two-hour delay was added between the training phase and the gambling phase (right set of bars).

A picture takes shape…

To summarise, we found that when people expected they might have to stop a motor response in a gambling task, they opted for less risky choices. And when we trained people to stop motor responses before doing the same gambling task, they also selected less risky options. This post-training aftereffect lasted for at least two hours. Overall then, these results indicate that these very different types of cognitive control are tightly coupled.  

Why such a link, you might ask. One possibility is that motor inhibition and risky decision-making draw on the same regulatory systems in the dorsolateral prefrontal cortex (DLPFC), a complex and mysterious part of the brain that coordinates a range of executive functions.

Of course, since these experiments are purely psychological, we can’t draw any conclusions about what might be changing in the DLPFC, but there are several possibilities to consider in future studies. For instance, recent work has found that more impulsive people tend to have lower levels of an inhibitory neurotransmitter called GABA in their DLPFC. Could motor cautiousness and inhibition training be somehow altering the expression of GABA in the DLPFC? Is motor cautiousness somehow tuning neural networks that regulate our behaviour, strengthening or biasing a computational ‘muscle’ that is used for decision-making? Perhaps inhibition training boosts the activity of DLPFC in regulating more primitive parts of the brain that respond to emotion and reward, such as the amygdala? Such questions are speculative, so to learn more we are now combining motor inhibition and gambling with a range of neuroscience methods, including transcranial magnetic stimulation (TMS), fMRI, simultaneous TMS-fMRI, and magnetic resonance spectroscopy.

As well as helping us understand more about cognitive control, our findings also have possible implications for treating gambling addiction. Related work by Katrijn Houben and Anita Jansen suggests that motor inhibition is linked to other compulsive behaviours, such as overeating and alcohol consumption. So could a regime of motor inhibition training help people overcome addiction? It seems possible, but we can’t claim from our results that motor inhibition provides a cure or treatment for any addiction. It is important to stress that all of the experiments in our study included healthy people only, and we currently have no data on whether motor inhibition training has any beneficial effect in a clinical situation. Furthermore, the effects we found are modest, just a 10-15% reduction in risk-taking. That said, we think the clinical angle is worth exploring and we may be able to tweak the design to make these effects larger and more clinically significant.

So can motor inhibition help us resist temptation? Possibly, yes. The next challenge is to figure out why and explore the implications – and applications – in clinical psychology and psychiatry.

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* All comments and questions are welcome.

* Thanks to Frederick Verbruggen for comments on a previous draft of this post.

* The press release associated with this study follows a new format arising from the recent Royal Institution debate we took part in on science and the media, hosted by Alok Jha and Alice Bell, and also featuring Ed Yong, Fiona Fox, and Ananyo Bhattacharya.