Tuesday, November 29, 2016

On Physics Envy

I followed my partner to a workshop in plasma physics. The workshop was held in a mountain resort in Poland – getting there was an adventure worthy, perhaps, of a separate blog post.

“I’m probably the only non-physicist in the room”, I say, apologetically, at the welcome reception, when professors come up to me to introduce themselves, upon seeing an unfamiliar face in the close-knit fusion community. 
Remembering this XKCD comic, I ask my partner: “How long do you think I could pretend to be a physicist for?” I clarify: “Let’s say, you are pretending to be a psychological scientist. I ask you what you’re working on. What would you say?”
“I’d say: ‘I’m working on orthographic depth and how affects reading processes, and also on statistical learning and its relationship to reading’.” Pretty good, that’s what I would say as well.
“So, if you’re pretending to be a physicist, what would you say if I ask you what you’re working on?”, he asks me.
“I’m, uh, trying to implement… what’s it called… controlled fusion in real time.”
The look on my partner’s face tells me that I would not do very well as an undercover agent in the physics community.

The attendees are around 50 plasma physicists, mostly greying, about three women among the senior scientist, perhaps five female post-docs or PhD students. Halfway through the reception dinner, I am asked about my work. In ten sentences, I try to describe what a cognitive scientist/psycholinguist does, trying to make it sound as scientific and non-trivial as possible. Several heads turn, curious to listen to my explanation. I’m asked if I use neuroimaging techniques. No, I don’t, but a lot of my colleagues and friends do. For the questions I’m interested in, anyway, I think we know too little about the relationship between brain and mind to make meaningful conclusions.
“It’s interesting”, says one physicist, “that you could explain to us what you are doing in ten sentences. For us, it’s much more difficult.” More people join in, admitting that they have given up trying to explain to their families what it is they are doing.
“Ondra gave me a pretty good explanation of what he is doing”, I tell them, pointing at my partner. I sense some scepticism. 

Physics envy is a term coined by psychologists (who else?), describing the inferiority complex associated with striving to be taken serious as a field in science. Physics is the prototypical hard science: they have long formulae, exact measurements where even the fifth decimal places matter, shiny multi-billion-dollar machines, and stereotypical crazy geniuses who would probably forget their own head if it wasn’t attached to them. Physicists don’t always make it easy for their scientific siblings (or distant cousins)* but, admittedly, they do have a right to be smug towards psychological scientists, given the replication crisis that we’re going through. The average physicist, unsurprisingly, finds it easier to grasp concepts associated with mathematics than the average psychologist. This means that physicist have, in general, a better understanding of probability. When I tell physicists about some of the absurd statements that some psychologists have made (“Including unpublished studies in the meta-analysis erroneously biases an effect size estimate towards zero.”; “Those replicators were just too incompetent to replicate our results. It’s very difficult to create the exact conditions under which we get the effect: even we had to try it ten times before we got this significant result!”), physicists start literally rolling on the floor with laughter. “Why do you even want to stay in this area of research?” I was asked once, after the physicist I was talking to had wiped off the tears of laughter. The question sounded neither rhetorical nor snarky, so I gave a genuine answer: “Because there are a lot of interesting questions that can be answered, if we improve the methodology and statistics we use.”

In physics, I am told, no experiment is taken seriously until it has been replicated by an independent lab. (Unless it requires some unique equipment, in which case it can't be replicated by an independent lab.) Negative results are still considered informative, unless they are due to experimental errors. Physicists still have issues with researchers who make their results look better than they actually are by cherry-picking the experimental results that fit best within one’s hypothesis and with post-hoc parameter adjustments – after all, the publish-or-perish system looms over all of academia. However, the importance of replicating results is a lesson that physicists have learnt from their own replication crisis: in the late 1980s, there was a shitstorm about cold fusion, set off by experimental results that were of immense public interest, but theoretically implausible, difficult to replicate, and later turned out to be due to sloppy research and/or scientific misconduct. (Sounds familiar?)

Physicists take their research very seriously, probably to a large extent because it is often of great financial interest. There are those physicists who work closely with industry. Even for those who don’t, their work often involves very expensive experiments. In plasma physics, a shot on the machine of Max Planck Institute for Plasma Physics, ASDEX-Upgrade, costs several thousand dollars. The number of shots required for an experiment depends on the research aims, and whether there is other data available, but can go up to 50 or more. This gives very strong motivation to make sure that one’s experiment is based on accurate calculations and sound theories which are supported by replicable studies. Furthermore, as there is only one machine – and only a handful of similar machines all over Europe – it needs to be shared with all other internal and external projects. In order to ensure that shots (and experimental time) are not wasted, any team wishing to perform an experiment needs to submit an application; the call for proposals opens only once a year. A representative of the team will also need to do a talk in front of the committee, which consists of the world’s leading experts in the area. The committee will decide whether the experiment is likely to yield informative and important results. In short, it is not possible – as in psychology – to spend one’s research career testing ideas one has on a whim, with twenty participants, and publish only if it actually ‘works’. One would be booed of the stage pretty quickly.

It’s easy to get into an us-and-them mentality and feelings of superiority and inferiority. No doubt all sciences have something of importance and of interest to offer to society in general. But it is also important to understand how we can maximise the utility of the research that we produce, and in this sense we can take a leaf out of physicists’ books. The importance of replication should be adopted also into the psychological literature: arguably, we should simply forget all theories that are based on non-replicable experiments. Perhaps more importantly, though, we should start taking our experiments more seriously. We need to increase our sample sizes; this conclusion seems to be gradually coming through as a consensus in psychological science. This means that also our experiments will become more expensive, both in terms of money and time. By conducting sloppy studies, we may still not loose thousands of dollars of taxpayers’ (or, even worse, investors’) money for each blotched experiment, but we will waste the time of our participants, the time, nerves and resources of researchers who try to make sense of or replicate our experiments, and we stall progress in our area of research, which has strong implications for policy makers in areas ranging from education through improving social equality, prisoners’ rehabilitation, and political/financial decision making, to mental health care.

* Seriously, though, I haven’t met a physicist who is as bad as the linked comic suggests.   

Acknowledgement: I'd like to thank Ondřej Kudláček, not only for his input into this blogpost and discussions about good science, but also for his unconditional support in my quest to learn about statistics.

Thursday, November 24, 2016

Flexible measures and meta-analyses: The case of statistical learning

On a website called flexiblemeasures.com, Malte Elson lists 156 dependent measures that have been used in the literature to quantify the performance on the Competitive Reaction Time Task. A task which has this many possible ways of calculating the outcome measure is, in a way, convenient for researchers: without correcting for multiple comparisons, the probability that the effect of interest will be significant in at least one of the measures skyrockets.

So does, of course, the probability that a significant result is a Type-I error (false positive). Such testing of multiple variables and reporting only the one which gives a significant result is an instance of p-hacking. It becomes problematic when another researcher tries to establish whether there is good evidence for an effect: if one performs a meta-analysis of the published analyses (using standardised effect sizes to be able to compare the different outcome measures across tasks), one can get a significant effect, even if each study reports only random noise and one creatively calculated outcome variable that ‘worked’.

Similarly, it becomes difficult for a researcher to establish how reliable a task is. Take, for example, statistical learning. Statistical learning, the cognitive ability to derive regularities from the environment and apply them to future events, has been linked to everything from language learning to autism. The concept of statistical learning ties to many theoretically interesting and practically important questions, for example, about how we learn, and what enables us to be able to use an abstract, complex system such as languages before we even learn to tie a shoelace.

Unsurprisingly, many tasks have been developed that are supposed to measure this cognitive ability of ours, and to correlate performance on these tasks to various everyday skills. Let us set aside the theoretical issues with the proposition that a statistical learning mechanism underlies the learning of statistical regularities in the environment, and concentrate on the way statistical learning is measured. This is an important question for someone who wants to study this statistical learning process: before running an experiment, one would like to be sure that the experimental task ‘works’.

As it turns out, statistical learning tasks don’t have particularly good psychometric properties: when the same individuals perform different tasks, the correlations between performance on different tasks are rather low; the test-retest reliability varies across tasks, but ranges from pretty good to pretty bad (Siegelman & Frost, 2015). For some tasks, performance on statistical learning tasks is not above chance for the majority of the participants, meaning that they cannot be used as valid indicators of individual differences in the statistical learning skill. This raises questions about why such a large proportion of published studies find that individual differences in statistical learning are correlated with various life-skills, and explains anecdotal evidence from myself and colleagues of conducting statistical learning experiments that just don’t work, in the sense that there is no evidence of statistical learning.* Relying on flexible outcome measures increases the researcher’s chances of finding a significant effect or correlation, which can be especially handy when the task has sub-optimal psychometric properties (low reliability and validity reduce the statistical power to find an effect if it exists). Rather than trying to improve the validity or reliability of the task, it is easier to continue analysing different variables until something becomes significant.

The first example of a statistical learning tasks is the Serial Reaction Time Task. Here, the participants respond to a series of stimuli, which appear on different positions on a screen. The participant presses buttons which correspond to the location of the stimulus. Unbeknown to the participant, the sequence of the locations repeats – the participants’ error rates and reaction times decrease. Towards the end of the experiment, normally in the penultimate block, the order of the locations is scrambled, meaning that the learned sequence is disrupted. Participants perform worse in this scrambled block compared to the sequential one. Possible outcome variables (which can all be found in the literature) are:
- Comparison of accuracy in the scrambled block to the preceding block
- Comparison of accuracy in the scrambled block to the succeeding (final) block
- Comparison of accuracy in the scrambled block compared to an average of the preceding and succeeding blocks
- The increase in accuracy across the sequential blocks
- Comparison of reaction times in the scrambled block to the preceding block
- Comparison of reaction times in the scrambled block to the succeeding (final) block
- Comparison of reaction times in the scrambled block compared to an average of the preceding and succeeding blocks
- The increase in reaction times across the sequential blocks.

This can hardly compare to the 156 dependent variables from the Competitive Reaction Time Task, but it already gives the researcher increased flexibility in selectively reporting only the outcome measures that ‘worked’. As an example of how this can lead to conflicting conclusions about the presence or absence of an effect: in a recent review, we discussed the evidence for a statistical learning deficit in developmental dyslexia (Schmalz, Altoè, & Mulatti, in press). In regards to the Serial Reaction Time Task, we concluded that there was insufficient evidence to decide whether or not there are differences in performance on this task across dyslexic participants and controls. Partly, this is because researchers tend to report different variables (presumably the one that ‘worked’): as it is rare for researchers to report the average reaction times and accuracy per block (or to respond to requests for raw data), it was impossible to pick the same dependent measure from all studies (say, the difference between the scrambled block and the one that preceded it) and perform a meta-analysis on it. Today, I stumbled across a meta-analysis on the same question: without taking into account differences between experiments in the dependent variable, Lum, Ullman, and Conti-Ramsden (2013) conclude that there is evidence for a statistical learning deficit in developmental dyslexia.

As a second example: in many statistical learning tasks, participants are exposed to a stream of stimuli which contain regularities. In a subsequent test phase, the participants then need to make decisions about stimuli which either follow the same patterns or not. This task can take many shapes, from a set of letter strings generated by a so-called artificial grammar (Reber, 1967) to strings of syllables with varying transitional probabilities (Saffran, Aslin, & Newport, 1996). It should be noted that both the overall accuracy rates (i.e., the observed rates of learning) and the psychometric properties varies across different variants of this tasks (see, e.g., Siegelman, Bogaerts, & Frost, 2016, who specifically aimed to create a statistical learning task with good psychometric properties). In these tasks, accuracy is normally too low to allow an analysis of reaction times; nevertheless, different dependent variables can be used: overall accuracy, the accuracy of grammatical items only, or the sensitivity index (d’). And, if there is imaging data, one can apparently interpret brain patterns in the complete absence of any evidence of learning on the behavioural level.

In summary, flexible measures could be an issue for evaluating the statistical learning literature: both in finding out which tasks are more likely to ‘work’, and in determining to what extent individual differences in statistical learning may be related to everyday skills such as language or reading. This does not mean that statistical learning does not exists, or that all existing work on this topic is flawed. However, it creates cause for healthy scepticism about the published results, and many interesting questions and challenges for future research. Above all, the field would benefit from increased awareness of issues such as flexible measures, which would lead to the pressure to increase the probability of getting a significant result by maximising the statistical power, i.e., decreasing the Type-II error rate (through larger sample sizes and more reliable and valid measures), rather than using tricks that affect the Type-I error rate.

Lum, J. A., Ullman, M. T., & Conti-Ramsden, G. (2013). Procedural learning is impaired in dyslexia: Evidence from a meta-analysis of serial reaction time studies. Research in Developmental Disabilities, 34(10), 3460-3476.
Reber, A. S. (1967). Implicit learning of artificial grammars. Journal of Verbal Learning and Verbal Behavior, 6(6), 855-863.
Saffran, J. R., Aslin, R. N., & Newport, E. L. (1996). Statistical learning by 8-month-old infants. Science, 274(5294), 1926-1928.
Schmalz, X., Altoè, G., & Mulatti, C. (in press). Statistical learning and dyslexia: a systematic review. Annals of Dyslexia. doi:10.1007/s11881-016-0136-0
Siegelman, N., Bogaerts, L., & Frost, R. (2016). Measuring individual differences in statistical learning: Current pitfalls and possible solutions. Behavior Research Methods, 1-15.
Siegelman, N., & Frost, R. (2015). Statistical learning as an individual ability: Theoretical perspectives and empirical evidence. Journal of Memory and Language, 81, 105-120.

* In my case, it’s probably a lack of flair, actually.

Wednesday, September 21, 2016

Some thoughts on methodological terrorism

Yesterday, I woke up to a shitstorm on Twitter, caused by an editorial-in-press by social psychologist Susan Fiske (who wrote my undergraduate Social Psych course textbook). The full text of the editorial, along with a superb commentary from Andrew Gelman, can be found here. This editorial, which launches an attack against so-called methodological terrorists who have the audacity to criticise their colleagues in public, has already inspired blog posts such as this one by Sam Schwarzkopf and this one which broke the time-space continuum by Dorothy Bishop

However, I would like to write about about one aspect of Susan Fiske’s commentary, which also emerged in a subsequent discussion with her at the congress of the German Society for Psychology (which, alas, I followed only on twitter). In the editorial Fiske states that psychological scientists at all stages of their career are being bullied; she seems especially worried about graduate students who are leaving academia. In the subsequent discussion, as cited by Malte Elson, she specifies that >30 graduate students wrote to her, in fear of cyberbullies.*

Being an early career researcher myself, I can try to imagine myself in a position where I would be scared of “methodological terrorists”. I can’t speak for all ECRs, but for what it’s worth, I don’t see any reason to stifle public debate. Of course, there is internet harassment which is completely inexcusable and should be punished (as covered by John Oliver in this video). But I have never seen, nor heard of, a scientific debate which dropped to the level of violence, rape or death threats.

So, what is the worst thing that can happen in academia? Someone finds a mistake in your work (or thinks they have found a mistake), and makes it public, either through the internet (twitter, blog), a peer-reviewed paper, or by screaming it out at an international conference after your talk. Of course, on a personal level, it is preferable that before or instead of making it public, the critic approaches you privately. On the other hand, the critic is not obliged to do this – as others build on your work, it is only fair that the public should be informed about a potential mistake. It is therefore, in practice, up to the critic to decide whether they will approach you first, or whether they think that a public approach would be more effective in getting an error fixed. Similarly, it would be nice of the critic to adopt a kind, constructive tone. It would probably make the experience more pleasant (or less unpleasant) for both parties, and be more effective in convincing the person who is criticised to think about the criticiser’s point and to decide rationally whether or not this is a valid point. But again, the critic is not obliged to be nice – someone who stands up at a conference to publicly destroy an early career researcher’s work is an a-hole, but not a criminal. (Though I can even imagine scenarios where such behaviour would be justified, for example, if the criticised researcher has been unresponsive to private expressions of concern about this work.)

As an early career researcher, it can be very daunting to face an audience of potential critics. It is even worse if someone accuses you of having done something wrong (whether it’s a methodological shortcoming of your experiment, or a possibly intentional error in your analysis script). I have received some criticism throughout my five-year academic career; some of it was not fair, though most of it was (even though I would sometimes deny it, in the initial stages). Furthermore, there are cultural differences in how researchers express their concern with some aspect of somebody’s work: in English-speaking countries (Australia, UK, US), much softer words seem to be used for criticising than in many mainland European countries (Italy, Germany). When I spent six months during my PhD in Germany, I was shocked at some of the conversations I had overheard between other PhD students and their supervisors – being used to the Australian style of conversation it seemed to me that German supervisors could be straight-out mean. Someone who is used to being told about a mistake with the phrase: “This is good, but you might want to consider…” is likely to be shocked and offended if they go to an international conference and someone tells them straight out: “This is wrong.” This could lead to some people feeling personally attacked due to what is more or less a cultural misunderstanding.

In any event, it is inevitable that one makes mistakes from time to time, and that someone finds something to criticise about your work. Indeed, this is how science progresses. We make mistakes, and we learn from them. We learn from others’ mistakes. Learning is what science is all about. Someone who doesn’t want to learn cannot be a scientist. And if nobody ever tells you that you made a mistake, you cannot learn from it. Yes, criticism stings, and some people are more sensitive than others. However, responding to criticism in a constructive way, and being aware of potential cultural differences in how criticism is conveyed, is part of the job description of an academic. Somebody who reacts explosively or defensively to criticism cannot be a scientist just like someone who is afraid of water cannot be an Olympic swimmer.

In response to this, Daniël Lakens wrote, in a series of tweets (I can’t phrase it better): “100+ students told me they think of quitting because science is no longer about science. [… They are the] ones you want to stay in science, because they are not afraid, they know what to do, they just doubt if a career in science is worth it.”

Monday, June 27, 2016

What happens when you try to publish a failure to replicate in 2015/2016

Anyone who has talked to me in the last year would have heard me complain about my 8-times-failure-to-replicate which nobody wants to publish. The preprint, raw data and analysis scripts are available here, so anyone can judge for themselves if they think the rejections to date are justified. In fact, if anyone can show me that my conclusions are wrong – that the data are either inconclusive, or that they actually support an opposite view – I will buy them a bottle of drink of their choice*. So far, this has not happened.

I promise to stop complaining about this after I publish this blog post. I think it is important to be aware of the current situation, but I am, by now, just getting tired of debates which go in circles (and I’m sure many others feel the same way). Therefore, I pledge that from now on I will stop writing whining blog posts, and I will only write happy ones – which have at least one constructive comment or suggestion about how we could improve things.

So, here goes my last ever complaining post. I should stress that the sentiments and opinions I describe here are entirely my own; although I’ve had lots of input from my wonderful co-authors in preparing the manuscript of my unfortunate paper, they would probably not agree with many of the things I am writing here.

Why is it important to publish failures to replicate?

People who haven’t been convinced by the arguments put forward to date will not be convinced by a puny little blogpost. In fact, they will probably not even read this. Therefore, I will not go into details about why it is important to publish failures to replicate. Suffice it to say that this is not my opinion – it’s a truism. If we combine a low average experimental power with selective publishing of positive results, we – to use Daniel Lakens’ words – get “a literature that is about as representative of real science as porn movies are representative of real sex”. We get over-inflated effect sizes across experiments, even if an effect is non-existent; or, in the words of Michael Inzlicht, “meta-analyses are fucked”.

Our study

The interested reader can look up further details of our study in the OSF folder I linked above (https://osf.io/myfk3/). The study is about the Psycholinguistic Grain Size Theory (Ziegler & Goswami, 2005)**. If you type the name of this theory into google – or some other popular search terms, such as “dyslexia theory”, “reading across languages”, or “reading development theory” – you will see this paper on the first page. It has 1650 citations, at the time of writing of this blogpost. In other words, this theory is huge. People rely on it to interpret their data, and to guide their experimental designs and theories in diverse topics of reading and dyslexia.

The evidence for the Psycholinguistic Grain Size Theory is summarised in the preprint linked above; the reader can decide for themselves if they find it convincing. During my PhD, I decided to do some follow-up experiments on the body-N effect (Ziegler & Perry, 1998; Ziegler et al., 2001; Ziegler et al., 2003). Why? Not because I wanted to build my career on the ruins of someone else’s work (which is apparently what some people think of replicators), but because I found the theory genuinely interesting, and I wanted to do further work to specify the locus of this effect. So I did study after study after study – blaming myself for the messy results – until I realised: I had conducted eight experiments, and the effect just isn’t there. So I conducted a meta-analysis on all of our data, plus an unpublished study by a colleague with whom I’d talked about this effect, wrote it up and submitted it.

Surely, in our day and age, journals should welcome null-results as much as positive results? And any rejections would be based on flaws in the study?

Well, here is what happened:

Submission 1: Relatively high-impact journal for cognitive psychology

Here is a section directly copied-and-pasted from a review:

“Although the paper is well-written and the analyses are quite substantial, I find the whole approach rather irritating for the following reasons:

1. Typically meta-analyses are done one [sic] published data that meet the standards for publishing in international peer-reviewed journals. In the present analyses, the only two published studies that reported significant effects of body-N and were published in Cognition and Psychological Science were excluded (because the trial-by-trial data were no longer available) and the authors focus on a bunch of unpublished studies from a dissertation and a colleague who is not even an author of the present paper. There is no way of knowing whether these unpublished experiments meet the standards to be published in high-quality journals.”

Of course, I picked the most extreme statement. Other reviewers had some cogent points – however, nothing that would compromise the conclusions. The paper was rejected because “the manuscript is probably too far from what we are looking for”.

Submission 2: Very high-impact psychology journal

As a very ambitious second plan, we submitted the paper to one of the top journals in psychology. It’s a journal which “publishes evaluative and integrative research reviews and interpretations of issues in scientific psychology. Both qualitative (narrative) and quantitative (meta-analytic) reviews will be considered, depending on the nature of the database under consideration for review” (from their website). They have even announced a special issue on Replicability and Reproducibility, because their “primary mission […] is to contribute a cohesive, authoritative, theory-based, and complete synthesis of scientific evidence in the field of psychology” (again, from their website). In fact, they published the original theoretical paper, so surely they would at least consider a paper which argues against this theory? As in, send it out for review? And reject it based on flaws, rather than the standard explanation of it being uninteresting to a broad audience? Given that they published the original theoretical article, and all? Right?

Wrong, on all points.

Submission 3: A well-respected, but not huge impact factor journal in cognitive psychology

I agreed to submit this paper to a non-open-access journal again, but only under the condition that at least one of my co-authors would have a bet with me: if it got rejected, I would get a bottle of good whiskey. Spoiler alert: I am now the proud owner of a 10-year aged bottle of Bushmills.

To be fair, this round of reviews brought some cogent and interesting comments. The first reviewer provided some insightful remarks, but their main concern was that “The main message here seems to be a negative one.” Furthermore, the reviewer “found the theoretical rationale [for the choice of paradigm] to be rather simplistic”. Your words, not mine! However, for a failure to replicate, this is irrelevant. As many researchers rely on what may or may not be a simplistic theoretical framework which is based on the original studies, we need to know whether the evidence put forward by the original studies is reliable.

I could not quite make sense of all of the second reviewer’s comment, but somehow they argued that the paper was “overkill”. (It is very long and dense, to be fair, but I do have a lot of data to analyse. I suspect most readers will skip from the introduction to the discussion, anyway – but anyone who wants the juicy details of the analyses should have easy access to them.)

Next step: Open-access journal

I like the idea of open-access journals. However, when I submitted previous versions of the manuscript I was somewhat swayed by the argument that going open access would decrease the visibility and credibility of the paper. This is probably true, but without any doubt, the next step will be to submit the paper to an open-access journal. Preferably one with open review. I would like to see a reviewer calling a paper “irritating” in a public forum.

At least in this case, traditional journals have shown – well, let’s just say that we still have a long way to go in improving replicability in psychological sciences. For now, I have uploaded a pre-print of the paper on OSF and on researchgate. On researchgate, the article has over 200 views, suggesting that there is some interest in this theory; the finding that the key study is not replicable seems relevant to researchers. Nevertheless, I wonder if the failure to provide support for this theory will ever gain as much visibility as the original study – how many researchers will put their trust into a theory that they might be more sceptical about if they knew the key study is not as robust as it may seem?

In the meantime, my offer of a bottle of beverage for anyone who can show that the analyses or data are fundamentally flawed, still stands.


* Beer, wine, whiskey, brandy: You name it. Limited only by my post-doc budget.
** The full references of all papers cited throughout the blogpost can be found in the preprint of our paper.


Edit 30/6: Thanks all for the comments so far, I'll have a closer look at how I can implement your helpful suggestions when I get the chance!

Please note that I will delete comments from spammers and trolls. If you feel the urge to threaten physical violence, please see your local counsellor or psychologist.

Thursday, June 16, 2016

Naming, not shaming: Criticising a weak result is not the same as launching a personal attack

You are working on a theoretical paper about the proposed relationship between X and Y. A two-experiment study has previously shown that X and Y are correlated, and you are trying to explain the cognitive mechanisms that drive this correlation. This previous study makes conclusions based on partial correlations which take into account a moderator that has not been postulated a priori; raw correlations are not reported. The p-values for each of the two partial correlations are < 0.05, but > 0.04. In a theoretical paper, you stress that although it makes theoretical sense that there would be a correlation between these variables, we cannot be sure about this link.

In a different paradigm, several studies have found a group difference in a certain task. In most studies, this group difference has a Cohen’s d of around 0.2. However, three studies which all come from the same lab report Cohen’s ds ranging between 0.8 and 1.1. You calculate that it is very unlikely to obtain three huge effects such as these by chance alone (probability < 1%). 

For a different project, you fail to find an effect which has been reported by a previously published experiment. The authors of this previous study have published their raw data a few years after the original paper came out. You take a close look at this raw data, and find some discrepancies with the means reported in the paper. When you analyse the raw data, the effect disappears.

What would you do in each of the scenarios above? I would be very happy to hear about it in the comments!

From each of these scenarios, I would draw two conclusions: (1) The evidence reported by these studies is not strong, to say the least, and (2) it is likely that the authors used what we now call questionable research practices to obtain significant results. The question is what we can conclude in our hypothetical paper, where the presence or absence of the effect is critical. Throwing around accusations of p-hacking can turn ugly. First, we cannot be absolutely sure that there is something fishy. Even if you calculate that the likelihood of obtaining a certain result is minimal, it is still greater than zero – you can never be completely sure that there really is something questionable going on. Second, criticising someone else’s work is always a hairy issue. Feelings may get hurt, and the desire for revenge may arise; careers can get destroyed. Especially as an early-career researcher, one wants to stay clear of close-range combat.

Yet, if your work rests on these results, you need to make something of them. One could just ignore them – not cite these papers, pretend they don’t exist. It is difficult to draw conclusions from studies with questionable research practices, so they may as well not be there. But ignoring relevant published work would be childish and unscientific. Any reader of your paper who is interested in the topic will notice this omission. Therefore, one needs to at least explain why one thinks the results of these studies may not be reliable.

One can’t explain why one doesn’t trust a study without citing it – a general phrase such as: “Previous work has shown this effect, but future research is needed to confirm its stability” will not do. We could remain general in our accusations: “Previous work has shown this effect (Lemmon & Matthau, 2000), but future research is needed to confirm its stability”. This, again, does not sound very convincing.

There are therefore two possibilities: either we drop the topic altogether, or we write down exactly why the results of the published studies would need to be replicated before we would trust them, kind of like what I did in the examples at the top of the page. This, of course, could be misconstrued as a personal attack. Describing such studies in my own papers is an exercise involving very careful phrasing and proofreading for diplomacy by very nice colleagues. Unfortunately, this often leads to the watering down of arguments, and tip-toeing around the real issue, which is the believability of a specific result. And when we think about it, this is what we are criticising – not the original researchers. Knowledge about questionable research practices is spreading gradually; many researchers are still in the process of realising that they can really damage a research area. Therefore, judging researchers for what they have done in the past would be neither productive, nor wise.

Should we judge a scientist for having used questionable research practices? In general, I don’t think so. I am convinced that the majority of researchers don’t intend to cheat, but they are convinced that they have legitimately maximised their chance to find a very small and subtle effect. It is, of course, the responsibility of a criticiser to make it clear that a problem is with the study, not with the researcher who conducted it. But the researchers whose work is being criticised should also consider whether the criticism is fair, and respond accordingly. If they are prepared to correct any mistakes – publishing file-drawer studies, releasing untrimmed data, conducting a replication, or in more extreme cases publishing a correction or even retracting a paper – it is unlikely that they will be judged negatively by the scientific community, quite on the contrary.

But there are a few hypothetical scenarios where my opinion of the researcher would decrease: (1) If the questionable research practice was data fabrication rather than something more benign such as creative outlier removal, (2) if the researchers use any means possible to suppress studies which criticise or fail to replicate their work, or (3) if the researchers continue to engage in questionable research practices, even after they learn that it increases their false-positive rate. This last point bears further consideration, because pleading ignorance is becoming less and less defensible. By now, a researcher would need to live under a rock if they have not even heard about the replication crisis. And a good, curious researcher should follow up on hearing such rumours, to check whether issues in replicability could also apply to them.

In summary, criticising existing studies is essential for scientific progress. Identifying potential issues with experiments will save time as researchers won’t go off on a wild-goose-chase for an effect that doesn’t exist; it will help us to narrow down on studies which need to be replicated before we consider that they are backed up by evidence. The criticism of a study, however, should not be conflated with criticism of the researcher – either by the criticiser or by the person being criticised. A strong distinction between the criticism of a study versus criticism of a researcher would result in a climate where discussions about reproducibility of specific studies will lead to scientific progress rather than a battlefield.

Saturday, May 21, 2016

What would the ideal research world look like?

Recently, I was asked: “What made you interested in research methods?” I’m afraid I didn’t give a good answer, but instead started complaining about my eight-times failure to replicate that nobody wants to publish. I have been thinking about this question some more, and realised that my interest in research methods and good science is driven by predominantly selfish reasons. This gave me the idea to write a blog post: I think it is important to realise that striving towards good science is, in the long run, beneficial to a researcher. So let’s ignore the “how” for the time being (there are already many articles and blog posts on this issue; see, for example, entries for an essay contest by The Winnower) – let’s focus on the “why”.

The world as it should be
Let’s imagine the research world as it should (or could) be. Presumably, we all went into research because we wanted to learn more about the world – and we wanted to actively contribute to discovering new knowledge. Imagine that we live in a world where we can trust the existing literature. Theories are based on experiments that are sound and replicable. The job of a researcher is to keep up to date on this literature, find gaps, and design experiments that can fill these gaps, thus providing a more complete picture of the phenomenon they are studying.

The world as it is
The research world as it is provides two sources of frustrations (at least, for me): (1) Playing Russian Roulette when it comes to conducting experiments, and (2) sifting through a literature which consists of an unknown ratio of manure to pearls, and trying to find the pearls.

Russian Roulette
I have conducted numerous experiments during my PhD and post-doc so far, and a majority of them “didn’t work”. By “didn’t work”, I mean they showed non-significant p-values when I expected an effect, showed different results from published experiments (again, my eight-times failure to replicate), and occasionally, they were just not designed very well and I would get floor/ceiling effects. I attributed this to my own lack of experience and competence. I looked to my colleagues had many published experiments, and considered alternative career paths. In the last year of my PhD, I came to a realisation: even professors have the same problem.

In the research world as it is, a researcher may come up with an idea for an experiment. It can be a great idea, based on a careful evaluation of theories and models. The experiment can be well-designed and neat, providing a pertinent test of the researcher’s hypothesis. Then the data is collected and analysed – and it is discovered that the experiment “didn’t work”. Shoulders are shrugged – the researcher moves on. Occasionally, one experiment will “work” and can be published.

How is it possible, I asked myself, that so much good research goes to waste, just because an experiment “didn’t work”? Is it really necessary to completely discard a promising question or theory, just because a first attempt at getting an answer “didn’t work”? How many labs conduct experiments that “don’t work”, not knowing that other labs have already tried and failed with the same approach? These are, as of now, rhetorical questions, but I firmly believe that learning more about research methods and how these can be used to produce sound and efficient experiments can answer them.

Sifting through manure
Some theories are intuitively appealing, apparently elegant, and elicit a lot of enthusiasm with a lot of people. New PhD students want to “do something with this theory”, and try to do follow-up studies, only to find that their follow-up experiments “don’t work”, replications of the experiments that support the theory “don’t work”, and the theory doesn’t even make sense when you really think about it. *

Scientists stand on the shoulders of giants. Science cannot be done without relying on existing knowledge at least to some extent. In an ideal world, our experiments and theories should build on previous work. However, I often get the feeling that I am building on manure instead of a sound foundation.

So, in order to try and understand whether I can trust an effect, I sift through the papers on it. I look for evidence of publication bias, dodgy-sounding post-hoc moderators or trimming decisions, statistical and logical errors (such as concluding that the difference between two groups is significant because one is significantly above chance while the other is not); check whether studies with larger sample sizes tend to give negative results, while positive results are predominantly supported by studies with small samples. It’s a thankless job. I criticise and question the work of colleagues, who are often in senior positions and may well one day make decisions that affect my livelihood. At the same time, I lack the time to conduct experiments to test and develop my own ideas. But what else should I do? Close my eyes to these issues and just work on my own line of research? Spending less or no time scrutinising the existing literature would mean that I don’t know whether I am building my research agenda on pearls or manure. This would mean that I could waste months or years on a question that I should have known to be a dead end from the very beginning.

So, why am I interested in research methods? Because it will make research more efficient, for me personally. It is difficult to conduct a good study, but in the long run, it should be no more difficult than running a number of crappy studies and publishing the one that “worked”. It should also be much less frustrating, much more rewarding, and in the end, we will do what we (presumably) love: contribute to discovering new knowledge about how the world works.


* This example is fictional. Any resemblance to real persons or events is purely coincidental.