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”.
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.
Monday, June 27, 2016
Thursday, June 16, 2016
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.