Sunday 24 March 2024

Just make it stop! When will we say that further research isn't needed?


I have a lifelong interest in laterality, which is a passion that few people share. Accordingly, I am grateful to René Westerhausen who runs the Oslo Virtual Laterality Colloquium, with monthly presentations on topics as diverse as chiral variation in snails and laterality of gesture production. 

On Friday we had a great presentation from Lottie Anstee who told us about her Masters project on handedness and musicality. There have been various studies on this topic over the years, some claiming that left-handers have superior musical skills, but samples have been small and results have been mixed. Lottie described a study with an impressive sample size (nearly 3000 children aged 10-18 years) whose musical abilities were evaluated on a detailed music assessment battery that included self-report and perceptual evaluations. The result was convincingly null, with no handedness effect on musicality. 

What happened next was what always happens in my experience when someone reports a null result. The audience made helpful suggestions for reasons why the result had not been positive and suggested modifications of the sampling, measures or analysis that might be worth trying. The measure of handedness was, as Lottie was the first to admit, very simple - perhaps a more nuanced measure would reveal an association? Should the focus be on skilled musicians rather than schoolchildren? Maybe it would be worth looking at nonlinear rather than linear associations? And even though the music assessment was pretty comprehensive, maybe it missed some key factor - amount of music instruction, or experience of specific instruments. 

After a bit of to and fro, I asked the question that always bothers me. What evidence would we need to convince us that there is really no association between musicality and handedness? The earliest study that Lottie reviewed was from 1922, so we've had over 100 years to study this topic. Shouldn't there be some kind of stop rule? This led to an interesting discussion about the impossibility of proving a negative and whether we should be using Bayes Factors, and what would be the smallest effect size of interest.  

My own view is that further investigation of this association would prove fruitless. In part, this is because I think the old literature (and to some extent the current literature!) on factors associated with handedness is at particular risk of bias, so even the messy results from a meta-analysis are likely to be over-optimistic. More than 30 years ago, I pointed out that laterality research is particularly susceptible to what we now call p-hacking - post hoc selection of cut-offs and criteria for forming subgroups, which dramatically increase the chances of finding something significant. In addition, I noted that measurement of handedness by questionnaire is simple enough to be included in a study as a "bonus factor", just in case something interesting emerges. This increases the likelihood that the literature will be affected by publication bias - the handedness data will be reported if a significant result is obtained, but otherwise can be disregarded at little cost. So I suspect that most of the exciting ideas about associations between handedness and cognitive or personality traits are built on shaky foundations, and would not replicate if tested in well-powered, preregistered studies.  But somehow, the idea that there is some kind of association remains alive, even if we have a well-designed study that gives a null result.  

Laterality is not the only area where there is no apparent stop rule. I've complained of similar trends in studies of association between genetic variants and psychological traits, for instance, where instead of abandoning an idea after a null study, researchers slightly change the methods and try again. In 2019, Lisa Feldman Barrett wrote amusingly about zombie ideas in psychology, noting that some theories are so attractive that they seem impossible to kill. I hope that as preregistration becomes more normative, we may see more null results getting published, and learn to appreciate their value. But I wonder just what it takes to get people to conclude that a research seam has been mined to the point of exhaustion. 

1 comment:

  1. Together with several colleagues we started a "Neuroimaging Zombies" project, out of the same frustration. We'd like to come up with strategies to expose a zombie, and also strategies to make your own studies easy to kill (instead of turning into a zombie). The availability of large open access datasets in neuroimaging should make it possible to create some general protective measures for many results. More info here: