I mentioned the issue of data quality before but reading Richard Morey’s interesting post about standardised effect sizes the other day made me think about this again. Yesterday I gave a lecture discussing Bem’s infamous precognition study and the meta-analysis he recently published of the replication attempts. I hadn’t looked very closely at the meta-analysis data before but for my lecture I produced the following figure:
This shows the standardised effect size for each of the 90 results in that meta-analysis split into four categories. On the left in red we have the ten results by Bem himself (nine of which are his original study and one is a replication of one of them by himself). Next, in orange we have what they call ‘exact replications’ in the meta-analysis, that is, replications that used his program/materials. In blue we have ‘non-exact replications’ – those that sought to replicate the paradigms but didn’t use his materials. Finally, on the right in black we have what I called ‘different’ experiments. These are at best conceptual replications because they also test whether precognition exists but use different experiment protocols. The hexagrams denote the means across all the experiments in each category (these are non-weighted means but it’s not that important for this post).
While the means for all categories are evidently greater than zero, the most notable thing should be that Bem’s findings are dramatically different from the rest. While the mean effect size in the other categories are below or barely at 0.1 and there is considerable spread beyond zero in all of them, all ten of Bem’s results are above zero and, with one exception, above 0.1. This is certainly very unusual and there are all sorts of reasons we could discuss for why this might be…
But let’s not. Instead let’s assume for the sake of this post that there is indeed such a thing as precognition and that Daryl Bem simply knows how to get people to experience it. I doubt that this is a plausible explanation in this particular case – but I would argue that for many kinds of experiments such “experimenter effects” are probably notable. In an fMRI experiment different labs may differ considerably in how well they control participants’ head motion or even simply in terms of the image quality of the MRI scans. In psychophysical experiments different experimenters may differ in how well they explain the task to participants or how meticulous they are in ensuring that they really understood the instructions, etc. In fact, the quality of the methods surely must matter in all experiments, whether they are in astronomy, microbiology, or social priming. Now this argument has been made in many forms, most infamously perhaps in Jason Mitchell’s essay “On the emptiness of failed replications” that drew much ire from many corners. You may disagree with Mitchell on many things but not on the fact that good methods are crucial. What he gets wrong is laying the blame for failed replications solely at the feet of “replicators”. Who is to say that the original authors didn’t bungle something up?
However, it is true that all good science should seek to reduce noise from irrelevant factors to obtain as clean observations as possible of the effect of interest. Using again Bem’s precognition experiments as an example, we could hypothesise that he indeed had a way to relax participants to unlock their true precognitive potential that others seeking to replicate his findings did not. If that were true (I’m willing to bet a fair amount of money that it isn’t but that’s not the point), if true, this would indeed mean that most of the replications – failed or successful – in his meta-analysis are only of low scientific value. All of these experiments are more contaminated by noise confounds than his experiments; thus only he provides clean measurements. Standardised effect sizes like Cohen’s d divide the absolute raw effect by a measure of uncertainty or dispersion in the data. The dispersion is a direct consequence of the noise factors involved. So it should be unsurprising that the effect size is greater for experimenters that are better at eliminating unnecessary noise.
Statistical inference seeks to estimate the population effect size from a limited sample. Thus, a meta-analytic effect size is an estimate of the “true” effect size from a set of replications. But since this population effect includes the noise from all the different experimenters, it does not actually reflect the true effect? The true effect is people’s inherent precognitive ability. The meta-analytic effect size estimate is spoiling that with all the rubbish others pile on with their sloppy Psi experimentation skills. Surely we want to know the former not the latter? Again, for precognition most of us will probably agree that this is unlikely – it seems more trivially explained by some Bem-related artifact – but in many situations this is a very valid point: Imagine one researcher manages to produce a cure for some debilitating disease but others fail to replicate it. I’d bet that most people wouldn’t run around shouting “Failed replication!”, “Publication bias!”, “P-hacking!” but would want to know what makes the original experiment – the one with the working drug – different from the rest.
The way I see that, meta-analysis of large scale replications is not the right way to deal with this problem. Meta-analysis of one lab’s replications are worthwhile, especially as a way to summarise a set of conceptually related experiments – but then you need to take them with a grain of salt because they aren’t independent replications. But large-scale meta-analysis across different labs don’t really tell us all that much. They simply don’t estimate the effect size that really matters. The same applies to replication efforts (and I know I’ve said this before). This is the point on which I have always sympathised with Jason Mitchell: you cannot conclude a lot from a failed replication. A successful replication that nonetheless demonstrates that the original claim is false is another story but simply failing to replicate some effect only tells you that something is (probably) different between the original and the replication. It does not tell you what the difference is.
Sure, it’s hard to make that point when you have a large-scale project like Brian Nosek’s “Estimating the reproducibility of psychological science” (I believe this is a misnomer because they mean replicability not reproducibility – but that’s another debate). Our methods sections are supposed to allow independent replication. The fact that so few of their attempts produced significant replications is a great cause for concern. It seems doubtful that all of the original authors knew what they were doing and so few of the “replicators” did. But in my view, there are many situations where this is not the case.
I’m not necessarily saying that large-scale meta-analysis is entirely worthless but I am skeptical that we can draw many firm conclusions from it. In cases where there is reasonable doubt about differences in data quality or experimenter effects, you need to test these differences. I’ve repeatedly said that I have little patience for claims about “hidden moderators”. You can posit moderating effects all you want but they are not helpful unless you test them. The same principle applies here. Rather than publishing one big meta-analysis after another showing that some effect is probably untrue or, as Psi researchers are wont to do, in an effort to prove that precognition, presentiment, clairvoyance or whatever are real, I’d like to see more attempts to rule out these confounds.
In my opinion the only way to do this is through adversarial collaboration. If an honest skeptic can observe Bem conduct his experiments, inspect his materials, and analyse the data for themselves and yet he still manages to produce these findings, that would go a much longer way convincing me that these effects are real than any meta-analysis ever could.
Data sharing has been in the news a lot lately from the refusal of the authors of the PACE trial to share their data even though the journal expects it to the eventful story of the “Sadness impairs color perception” study. A blog post by Dorothy Bishop called “Who’s afraid of Open Data?” made the rounds. The post itself is actually a month old already but it was republished by the LSE blog which gave it some additional publicity. In it she makes a impassioned argument for open data sharing and discusses the fears and criticisms many researchers have voiced against data sharing.
I have long believed in making all data available (and please note that in the following I will always mean data and materials, so not just the results but also the methods). The way I see it this transparency is the first and most important remedy to the ills of scientific research. I have regular discussions with one of my close colleagues* about how to improve science – we don’t always agree on various points like preregistration, but if there is one thing where we are on the same page, it is open data sharing. By making data available anyone can reanalyse it and check if the results reproduce and it allows you to check the robustness of a finding for yourself, if you feel that you should. Moreover, by documenting and organising your data you not only make it easier for other researchers to use, but also for yourself and your lab colleagues. It also helps you with spotting errors. It is also a good argument that stops reviewer 2 from requesting a gazillion additional analyses – if they really think these analyses are necessary they can do them themselves and publish them. This aspect in fact overlaps greatly with the debate on Registered Reports (RR) and it is one of the reasons I like the RR concept. But the benefits of data sharing go well beyond this. Access to the data will allow others to reuse the data to answer scientific questions you may not even have thought of. They can also be used in meta-analyses. With the increasing popularity and feasibility of large-scale permutation/bootstrapping methods it also means that availability to the raw values will be particularly important. Access to the data allows you to take into account distributional anomalies, outliers, or perhaps estimate the uncertainty on individual data points.
But as Dorothy describes, many scientists nevertheless remain afraid of publishing their actual data alongside their studies. For several years many journals and funding agencies have had a policy that data should always be shared upon request – but a laughably small proportion of such requests are successful. This is why some have now adopted the policy that all data must be shared in repositories upon publication or even upon submission. And to encourage this process recently the Peer Reviewer Openness Initiative was launched by which signatories would refuse to conduct in-depth reviews of manuscripts unless the authors can give a reason why data and materials aren’t public.
My most memorable experience with fears about open data involve a case where the lab head refused to share data and materials with the graduate student* who actually created the methods and collected the data. The exact details aren’t important. Maybe one day I will talk more about this little horror story… For me this demonstrates how far we have come already. Nowadays that story would be baffling to most researchers but back then (and that’s only a few years ago – I’m not that old!) more than one person actually told me that the PI and university were perfectly justified in keeping the student’s results and the fruits of their intellectual labour under lock and key.
Clearly, people are still afraid of open data. Dorothy lists the following reasons:
Lack of time to curate data; Data are only useful if they are understandable, and documenting a dataset adequately is a non-trivial task;
Personal investment – sense of not wanting to give away data that had taken time and trouble to collect to other researchers who are perceived as freeloaders;
Concerns about being scooped before the analysis is complete;
Fear of errors being found in the data;
Ethical concerns about confidentiality of personal data, especially in the context of clinical research;
Possibility that others with a different agenda may misuse the data, e.g. perform selective analysis that misrepresented the findings;
In my view, points 1-4 are invalid arguments even if they seem understandable. I have a few comments about some of these:
The fear of being scooped
I honestly am puzzled by this one. How often does this actually happen? The fear of being scooped is widespread and it may occasionally be justified. Say, if you discuss some great idea you have or post a pilot result on social media perhaps you shouldn’t be surprised if someone else agrees that the idea is great and also does it. Some people wouldn’t be bothered by that but many would and that’s understandable. Less understandable to me is if you present research at a conference and then complain about others publishing similar work because they were inspired by you. That’s what conferences are for. If you don’t want that to happen, don’t go to conferences. Personally, I think science would be a lot better if we cared a lot less about who did what first and instead cared more about what is true and how we can work together…
But anyway, as far as I can see none of that applies to data sharing. By definition data you share is either already published or at least submitted for peer review. If someone reuses your data for something else they have to cite you and give you credit. In many situations they may even do it in collaboration with you which could lead to coauthorship. More importantly, if the scooped result is so easily obtained that somebody beats you to it despite your head start (it’s your data, regardless of how well documented it is you will always know it better than some stranger) then perhaps you should have thought about that sooner. You could have held back on your first publication and combined the analyses. Or, if it really makes more sense to publish the data in separate papers, then you could perhaps declare that the full data set will be shared after the second one is published. I don’t really think this is necessary but I would accept that argument.
Either way, I don’t believe being scooped by data sharing is very realistic and any cases of that happening must be extremely rare. But please share these stories if you have them to prove me wrong! If you prefer, you can post it anonymously on the Neuroscience Devils. That’s what I created that website for.
Fear of errors being discovered
I’m sure everyone can understand that fear. It can be embarrassing to have your errors (and we all make mistakes) being discovered – at least if they are errors with big consequences. Part of the problem is also that all too often the discovery of errors is associated with some malice. To err is human, to forgive divine. We really need to stop treating every time somebody’s mistakes are being revealed (or, for that matter, when somebody’s findings fail to replicate) as an implication of sloppy science or malpractice. Sometimes (usually?) mistakes are just mistakes.
Probably nobody wants to have all of their data combed by vengeful sleuths nitpicking every tiny detail. If that becomes excessive and the same person is targeted, it could border on harassment and that should be counteracted. In-depth scrutiny of all the data by a particular researcher should be a special case that only happens when there is a substantial reason, say, in a fraud investigation. I would hope though that these cases are also rare.
And surely nobody can seriously want the scientific record to be littered with false findings, artifacts, and coding errors. I am not happy if someone tells me I made a serious error but I would nonetheless be grateful to them for telling me! It has happened before when lab members or collaborators spotted mistakes I made. In turn I have spotted mistakes colleagues made. None of this would have been possible if we didn’t share our data and methods amongst each another. I am always surprised when I hear how uncommon this seems to be in some labs. Labs should be collaborative, and so should science as a whole. And as I already said, organising and documenting your data actually helps you to spot errors before the work is published. If anything, data sharing reduces mistakes.
Ethical issues with patient confidentiality
This is a big concern – and the only one that I have full sympathy with. But all of our ethics and data protection applications actually discuss this. The only data that is shared should be anonymised. Participants should only be identified by unique codes that only the researchers who collected the data have access to. For a lot of psychology or other behavioural experiments this shouldn’t be hard to achieve.
Neuroimaging or biological data are a different story. I have a strict rule for my own results. We do not upload the actual brain images of our fMRI experiments to public repositories. While under certain conditions I am willing to share such data upon request as long as the participant’s name has been removed, I don’t think it is safe to make those data permanently available to the entire internet. Participant confidentiality must trump the need for transparency. It simply is not possible to remove all identifying information from these files. Skull-stripping, which removes the head tissues from an MRI scan except for the brain, does not remove all identifying information. Brains are like finger-prints and they can easily be matched up, if you have the required data. As someone* recently said in a discussion of this issue, the undergrad you are scanning in your experiment now may be Prime Minister in 20-30 years time. They definitely didn’t consent to their brain scans being available to anyone. It may not take much to identify a person’s data using only their age, gender, handedness, and a basic model of their head shape derived from their brain scan. We must also keep in mind of what additional data mining may be possible in the coming decades that we simply have no idea about yet. Nobody can know what information could be gleaned from these data, say, about health risks or personality factors. Sharing this without very clear informed consent (that many people probably wouldn’t give) is in my view irresponsible.
I also don’t believe that for most purposes this is even necessary. Most neuroimaging studies involve group analyses. In those you first spatially normalise the images of each participant and the perform statistical analysis across participants. It is perfectly reasonable to make those group results available. For purpose of non-parametric permutation analyses (also in the news recently) you would want to share individual data points but even there you can probably share images after sufficient processing that not much incidental information is left (e.g. condition contrast images). In our own work, these considerations don’t apply. We conduct almost all our analyses in the participant’s native brain space. As such we decided to only share the participants’ data projected on a cortical reconstruction. These data contain the functional results for every relevant voxel after motion correction and signal filtering. No this isn’t raw data but it is sufficient to reproduce the results and it is also sufficient for applying different analyses. I’d wager that for almost all purposes this is more than enough. And again, if someone were to be interested in applying different motion correction or filtering methods, this would be a negotiable situation. But I don’t think we need to allow unrestricted permanent access for such highly unlikely purposes.
Basically, rather than sharing all raw data I think we need to treat each data set on a case-by-case basis and weigh the risks against benefits. What should be mandatory in my view is sharing all data after default processing that is needed to reproduce the published results.
People with agendas and freeloaders
Finally a few words about a combination of points 2 and 6 in Dorothy Bishop’s list. When it comes to controversial topics (e.g. climate change, chronic fatigue syndrome, to name a few examples where this apparently happened) there could perhaps be the danger that people with shady motivations will reanalyse and nitpick the data to find fault with them and discredit the researcher. More generally, people with limited expertise may conduct poor reanalysis. Since failed reanalysis (and again, the same applies to failed replications) often cause quite a stir and are frequently discussed as evidence that the original claims were false, this could indeed be a problem. Also some will perceive these cases as “data tourism”, using somebody else’s hard-won results for quick personal gain – say by making a name for themselves as a cunning data detective.
There can be some truth in that and for that reason I feel we really have to work harder to change the culture of scientific discourse. We must resist the bias to agree with the “accuser” in these situations. (Don’t pretend you don’t have this bias because we all do. Maybe not in all cases but in many cases…)
Of course skepticism is good. Scientists should be skeptical but the skepticism should apply to all claims (see also this post by Neuroskeptic on this issue). If somebody reanalyses somebody else’s data using a different method that does not automatically make them right and the original author wrong. If somebody fails to replicate a finding, that doesn’t mean that finding was false.
Science thrives on discussion and disagreement. The critical thing is that the discussion is transparent and public. Anyone who has an interest should have the opportunity to follow it. Anyone who is skeptical of the authors’ or the reanalysers’/replicators’ claims should be able to check for themselves.
And the only way to achieve this level of openness is Open Data.
* They will remain anonymous unless they want to join this debate.
TL;DR: Claiming that something is “selective” implies knowledge of the stimulus dimension to which it is tuned. It also does not apply to simple intensity codes because selectivity requires a tuning preference.
This post is a just little rant about an age-old pet peeve of mine: neuroscience studies claiming they found that some brain area is selective for some stimulus/task/mental state etc. This issue recently resurfaced in my mind because of an interesting exchange between Tal Yarkoni on the one hand and Matt Lieberman and Naomi Eisenberger on the other. The latter recently published a study in PNAS suggesting that dACC is “selective for pain”. Yarkoni wrote a detailed rebuttal to their claims criticising the way they inferred selectivity. I recommend following this on-going discourse (response by Lieberman & Eisenberger and a response to their response by Yarkoni). I won’t go into any depth on it here. Rather I want to make a more general comment on why I feel the term selectivity is frequently misused.
Neuroimaging methods like fMRI allow researchers to localise brain regions that respond preferentially to particular stimuli or tasks. This “blobology” is becoming less common now that our field has matured and many experiments are more sophisticated. Nevertheless, localising brain regions that respond more to one experimental condition than another will probably remain a common sight in the neuroimaging literature for a long time to come, even if the most typical such use is probably functional localisers to limit the regions of interest in more complex experiments.
Anyway, in blobological studies, results are frequently reported as showing that your blob is “selective” for something or other: not only are we supposed to believe that the dACC is selective for pain, but also that the FFA is selective for images of faces, the LOC is selective for intact objects, and the MT+ complex is selective for motion. While some of these claims may be correct, they are not demonstrated by blobology using any kind of method. In fact, Lieberman and Eisenberger write in their response to Yarkoni:
“We’ve never seen a response to one of these papers that says they were wrong to make these claims because they didn’t test for the thousands of other things the region of interest might respond to. Thus the weak form of selectivity, the version we were using, can be stated this way:
Selectivityweak: The dACC is selective for pain, if pain is a more reliable source of dACC activation than the other terms of interest (executive, conflict, salience).”
Perhaps there has never been a response saying that these were wrong but I think there should have. What is selectivity? While the dictionary defines “selective” as a synonym of
“discriminating, particular, discerning”
the term has long been established in neuroscience. Take the Nobel Prize winning research by Hubel and Wiesel in the 1960s for example. They discovered that neurons in the visual cortex are selective to the orientation of simple bar stimuli. So for instance a horizontal bar may drive a neuron to fire strongly while a vertical one would not. In the neurophysiology literature one would say that this particular neuron has an “preference” for horizontal bars.
This, however, does not mean that the neuron is “selective” for horizontal bars. The firing rate in response to oblique bars is likely somewhere between the rate for horizontal and vertical ones. The distinction between preference and selectivity may seem like semantic quibbling but it’s not. They are referring to very different concepts and, as I will try to argue, this distinction is important. But let’s not jump ahead.
“Strong” selectivity (to use Lieberman and Eisenberger’s terminology) implies that the neuron only responds to horizontal bars but not much else. In the following images, the contrast of each oriented grating denotes how much of a neuronal response it would produce.
A “weakly” selective neuron might respond similarly across a wide range of orientations:
An even less selective neuron would show very similar responses to all orientations and a completely non-selective neuron would respond at the same rate to any visual stimulus regardless of its orientation.
This means we can measure responses of the neuron across the whole range of orientations (or, more generally speaking, across a range of different stimulus values). Thus we can determine not only the preferred orientation but also how strongly the exact orientation modulates neuronal responses. In other words, we can quantify how discerning, how selective the neuron is for orientation. The key point here is that in all these examples the stimulus dimension for which the neuron is selective is the orientation of bar stimuli. The neuron prefers horizontal. It is selective for orientation.
So at least according to how neurophysiologists have defined selectivity over the past half century, the term refers to how much varying the stimulus along this dimension affects the neuronal response. I hope you will agree now that this does not apply to many of the claims of selectivity in the neuroimaging literature: an experiment that shows stronger responses in FFA to faces than houses shows that FFA prefers faces. It does not show that it doesn’t also prefer other stimuli, a point already discussed by Tarkoni and Lieberman and Eisenberger. More importantly, it does not demonstrate that FFA is selective for faces.
Rather the stimulus dimension for which there may be selectivity here could be loosely categorised as “visual objects” or even just “images”. Face-selectivity implies that the region is sensitive to changing the face identity (or possibly also some other attribute specific to faces). Now, I believe there is fairly good evidence that FFA does just that – however, simply comparing the response to faces to non-face images does not and cannot possibly demonstrate this. Only comparing responses (or response patterns) to different faces can achieve that.
Why does this matter? Is this really not mere semantics? No, because from all of this follows that to demonstrate selectivity requires systematic manipulation of the stimulus space. You must map out how changing the stimulus modulates responses by a neuron or brain region or whatever. You cannot make any claim about selectivity without any concept of how different stimuli relate to each other. For orientation that is simple but for more complex objects it is not. Comparing faces to houses or body parts or animals or tools or whatnot cannot achieve that, not unless you can tell me exactly why one category (say, houses?) should be more similar to faces than another (say, cars?). There are many possible models that could relate different categories. It could be based on low-level visual similarity, semantic similarity, conceptual similarity, etc. There are studies investigating exactly that, for example by using representational similarity analysis – but a discussion of this is outside the scope of this post. The point is that simply randomly comparing different object categories, no matter how many thousands, does not by itself tell you about selectivity.
Hopefully, by now I have convinced you why the claim that the dACC is selective for pain cannot possibly be correct, at least not if it is based only on a blobological method comparing responses to an arbitrary set of stimuli. I am not even sure that selectivity for pain is even conceptually possible. It would imply that there are mental states or tasks that are just not quite pain but not really something else yet either, and that there is a systematic relationship between that and dACC responses. Perhaps this is possible, I don’t know. Either way, no fMRI or NeuroSynth or other analysis comparing pain and rejection and conflict resolution or whatever can demonstrate this.
While we’re at it, showing that responses in dACC covary with the intensity of pain would not confirm selectivity for pain either. All that this shows is that dACC is responsive to pain. Because stimulus selectivity and preference go hand in hand. Selectivity for pain would imply that this region preferentially responds to a particular pain level but less so to pain that is stronger or weaker.
I added another paragraph because of a discussion I had about this last point on social media: selectivity implies that a neuron or brain area is tuned to a stimulus space and it can only exist if there is also a stimulus preference. An intensity code merely implies that responses increase as the stimulus quantity is increased. While the steepness of this increase can vary and tells you about sensitivity, such a neuron has no stimulus preference because the response either saturates (thus losing sensitivity beyond a certain level) or increases linearly (which is probably biologically implausible). This is mechanistically different from selectivity with different consequences on how the stimulus dimension is represented and how it affects behaviour. A brain area may very well be sensitive to contrast, to pain intensity, or confidence – but unless the code allows you to infer the exact stimulus level from the response it isn’t selective.
Finally buckled and got myself a new domain and got rid of the infernal ads on this page. I may eventually do the same for my official lab webpage although there ads are only an issue if you’re foolish enough to click on one of the posts so I may hold off on it.
TL;DR: Leave-one-out cross-validation is a bad way for testing the predictive power of linear correlation/regression.
Correlation or regression analysis are popular tools in neuroscience and psychology research for analysing individual differences. It fits a model (most typically a linear relationship between two measures) to infer whether the variability in some measure is related to the variability in another measure. Revealing such relationships can help understand the underlying mechanisms. We and others used it in previous studies to test specific mechanistic hypotheses linking brain structure/function and behaviour. It also forms the backbone of twin studies of heritability that in turn can implicate genetic and experiential factors in some trait. Most importantly, in my personal view individual differences are interesting because they acknowledge the fact that every human being is unique rather than simply treating variability as noise and averaging across large groups people.
But typically every report of a correlational finding will be followed by someone zealously pointing out that “Correlation does not imply causation”. And doubtless it is very important to keep that in mind. A statistical association between two variables may simply reflect the fact that they are both related to a third, unknown factor or a correlation may just be a fluke.
Another problem is that the titles of studies using correlation analysis sometimes use what I like to call “smooth narrative” style. Saying that some behaviour is “predicted by” or “depends on” some brain measure makes for far more accessible and interesting reading that dryly talking about statistical correlations. However, it doesn’t sit well with a lot of people, in part because such language may imply a causal link that the results don’t actually support. Jack Gallant seems to regularly point out on Twitter that the term “prediction” should only ever be used when a predictive model is built on some data set but the validity is tested on an independent data set.
Recently I came across an interesting PubPeer thread debating this question. In this one commenter pointed out that the title of the study under discussion, “V1 surface size predicts GABA concentration“, was unjustified because this relationship explains only about 7% of the variance when using a leave-one-out cross-validation procedure. In this procedure all data points except one are used to fit the regression and the final point is then used to evaluate the fit of the model. This procedure is then repeated n-fold using every data point as evaluation data once.
Taken at face value this approach sounds very appealing because it uses independent data for making predictions and for testing them. Replication is a cornerstone of science and in some respects cross-validation is an internal replication. So surely this is a great idea? Naive as I am I have long had a strong affinity for this idea.
Cross-validation underestimates predictive power
But not so fast. These notions fail to address two important issues (both of which some commenters on that thread already pointed out): first, it is unclear what amount of variance a model should explain to be important. 7% is not very much but it can nevertheless be of substantial theoretical value. The amount of variance that can realistically be explained by any model is limited by the noise in the data that arises from measurement error or other distortions. So in fact many studies using cross-validation to estimate the variance explained by some models (often in the context of model comparison) instead report the amount of explainable variance accounted for by the model. To derive this one must first estimate the noise ceiling, that is, the realistic maximum of variance that can possibly be explained. This depends on the univariate variability of the measures themselves.
Second, the cross-validation approach is based on the assumption that the observed sample, which is then subdivided into model-fitting and evaluation sets, is a good representation of the population parameters the analysis is attempting to infer. As such, the cross-validation estimate also comes with an error (this issue is also discussed by another blog post mentioned in that discussion thread). What we are usually interested in when we conduct scientific studies is to make an inference about the whole population, say a conclusion that can be broadly generalised to any human brain, not just the handful of undergraduate students included in our experiments. This does not really fit the logic of cross-validation because the evaluation is by definition only based on the same sample we collected.
Because I am a filthy, theory-challenged experimentalist, I decided to simulate this (and I apologise to all my Bayesian friends for yet again conditioning on the truth here…). For a range of sample sizes between n=3 and n=300 I drew a sample with from a population with a fixed correlation of rho=0.7 and performed leave-one-out cross-validation to quantify the variance explained by it (using the squared correlation between predicted and observed values). I also performed a standard regression analysis and quantified the variance explained by that. At each sample size I did this 1000 times and then calculated the mean variance explained for each approach. Here are the results:
What is immediately clear is that the results strongly depend on the sample size. Let’s begin with the blue line. This represents the variance explained by the standard regression analysis on the whole observed sample. The dotted, black, horizontal line denotes the true effect size, that is, the variance explained by the population correlation (so R^2=49%). The blue line starts off well above the true effect but then converges on it. This means that at small sample sizes, especially below n=10, the observed sample inflates how much variance is explained by the fitted model.
Next look at the red line. This denotes the variance explained by the leave-one-out cross-validation procedure. This also starts off above the true population effect and follows the decline of the observed correlation. But then it actually undershoots and goes well below the true effect size. Only then it gradually increases again and converges on the true effect. So at sample sizes that are most realistic in individual differences research, n=20-100ish, this cross-validation approach underestimates how much variance a regression model can explain and thus in fact undervalues the predictive power of the model.
The error bars in this plot denote +/- 1 standard deviation across the simulations at each sample size. So as one would expect, the variability across simulations is considerable when sample size is small, especially when n <= 10. These sample sizes are maybe unusually small but certainly not unrealistically small. I have seen publications calculating correlations on such small samples. The good news here is that even with such small samples on average the effect may not be inflated massively (let’s assume for the moment that publication bias or p-hacking etc are not an issue). However, cross-validation is not reliable under these conditions.
A correlation of rho=0.7 is unusually strong for most research. So I repeated this simulation analysis using a perhaps more realistic effect size of rho=0.3. Here is the plot:
Now we see a hint of something fascinating: the variance explained by the cross-validation approach actually subtly exceeds that of the observed sample correlation. They again converge on the true population level of 9% when the sample size reaches n=50. Actually there is again an undershoot but it is negligible. But at least for small samples with n <= 10 the cross-validation certainly doesn’t perform any better than the observed correlation. Both massively overestimate the effect size.
When the null hypothesis is true…
So if this is what is happening at a reasonably realistic rho=0.3, what about when the null hypothesis is true? This is what is shown in here (I apologise for the error bars extending into the impossible negative range but I’m too lazy to add that contingency to the code…):
The problem we saw hinted at above for rho=0.3 is exacerbated here. As before, the variance explained for the observed sample correlation is considerably inflated when sample size is small. However, for the cross-validated result this situation is much worse. Even at a sample size of n=300 the variance explained by the cross-validation is greater than 10%. If you read the PubPeer discussion I mentioned, you’ll see that I discussed this issue. This result occurs because when the null hypothesis is true – or the true effect is very weak – the cross-validation will produce significant correlations between the inadequately fitted model predictions and the actual observed values. These correlations can be positive or negative (that is, the predictions systematically go in the wrong direction) but because the variance explained is calculated by squaring the correlation coefficient they turn into numbers substantially greater than 0%.
As I discussed in that thread, there is another way to calculate the variance explained by the cross-validation. I won’t go into detail on this but unlike the simpler approach I employed here this does not limit the variance explained to fall between 0-100%. While the estimates are numerically different, the pattern of results is qualitatively the same. At smaller sample sizes the variance explained by cross-validation systematically underestimates the true variance explained.
When the interocular traumatic test is significant…
My last example is the opposite scenario. While we already looked at an unusually strong correlation, I decided to also simulate a case where the effect should be blatantly obvious. Here rho=0.9:
Unsurprisingly, the results are similar as those seen for rho=0.7 but now the observed correlation is already doing a pretty decent job at reaching the nominal level of 81% variance explained. Still, the cross-validation underperforms at small sample sizes. In this situation, this actually seems to be a problem. It is rare that one would observe a correlation of this magnitude in psychological or biological sciences but if so chances are good that the sample size is small in that case. Often the reason for this may be that correlation estimates are inflated at small sample sizes but that’s not the point here. The point is that leave-one-out cross-validation won’t tell you. It underestimates the association even if it is real.
Where does all this leave us?
It is not my intention to rule out cross-validation. It can be a good approach for testing models and is often used successfully in the context of model comparison or classification analysis. In fact, as the debate about circular inference in neuroscience a few years ago illustrated, there are situations where it is essential that independent data are used. Cross-validation is a great way to deal with overfitting. Just don’t let yourself be misled into believing it can tell you something it doesn’t. I know it is superficially appealing and I had played with it previously for just that reason – but this exercise has convinced me that it’s not as bullet-proof is one might think.
Obviously, validation of a model with independent data is a great idea. A good approach is to collect a whole independent replication sample but this is expensive and may not always be feasible. Also, if a direct replication is performed it seems better that this is acquired independently by different researchers. A collaborative project could do this in which each group uses the data acquired by the other group to test their predictive model. But that again is not something that is likely to become regular practice anytime soon.
In the meantime we can also remember that performing typical statistical inference is a good approach after all. Its whole point is to infer the properties of the whole population from a sample. When used properly it tends to do a good job at that. Obviously, we should take measures to improve its validity, such as increasing power by using larger samples and/or better measurements. I know I am baysed but Bayesian hypothesis tests seem superior at ensuring validity than traditional significance testing. Registered Reports can probably also help and certainly should reduce the skew by publication bias and flexible analyses.
So, does correlation imply prediction? I think so. Statistically this is precisely what it does. It uses one measure (or multiple measures) to make predictions of another measure. The key point is not whether calling it a prediction is valid but whether the prediction is sufficiently accurate to be important. The answer to this question actually depends considerably on what we are trying to do. A correlation explaining 10-20% of the variance in a small sample is not going to be a clear biomarker for anything. I sure as hell wouldn’t want any medical or judicial decisions to be based solely on such an association. But it may very well be very informative about mechanisms. It is a clearly detectable effect even with the naked eye.
In the context of these analysis, a better way than quantifying the variance explained is to calculate the root mean squared deviation (essentially the error bar) of the prediction. This provides an actually much more direct index of how accurately one variable predicts another. The next step – and I know I sound like a broken record – should be to confirm that these effects are actually scientifically plausible. This mantra is true for individual differences research as much as it is for Bem’s precognition and social priming experiments where I mentioned it before. Are the differences in neural transmission speed or neurotransmitter concentration implied by these correlation results realistic based on what we know about the brain? These are the kinds of predictions we should actually care about in these discussions.
In my previous post, I talked about why I think all properly conducted research should be published. Null results are important. The larger scientific community needs to know whether or not a particular hypothesis has been tested before. Otherwise you may end up wasting somebody’s time because they repeatedly try in vain to answer the same question. What is worse, we may also propagate false positives through the scientific record because failed replications are often still not published. All of this contributes to poor replicability of scientific findings.
However, the emphasis here is on ‘properly conducted research‘. I already discussed this briefly in my post but it also became the topic of an exchange between (for the most part) Brad Wyble, Daniël Lakens, and myself. In some fields, for example psychophysics, extensive piloting, and “fine-tuning” of experiments is not only very common but probably also necessary. To me it doesn’t seem sensible to make the results of all of these attempts publicly available. This inevitably floods the scientific record with garbage. Most likely nobody will look at it. Even if you are a master at documenting your work, nobody but you (and after a few months maybe not even you) will understand what is in your archive.
Most importantly, it can actually be extremely misleading for others who are less familiar with the experiment to see all of the tests you did ensuring the task was actually doable, that monitors were at the correct distance from the participant, your stereoscope was properly aligned, the luminance of the stimuli was correct, that the masking procedure was effective, etc. Often you may only realise during your piloting that the beautiful stimulus you designed after much theoretical deliberation doesn’t really work in practice. For example, you may inadvertently induce an illusory percept that alters how participants respond in the task. This in fact happened recently with an experiment a collaborator of mine piloted. And more often than not, after having tested a particular task on myself at great length I then discover that it is far too difficult for anyone else (let’s talk about overtrained psychophysicists another time…).
Such pilot results are not very meaningful
It most certainly would not be justified to include them in a meta-analysis to quantify the effect – because they presumably don’t even measure the same effect (or at least not very reliably). A standardised effect size, like Cohen’s d, is a signal-to-noise ratio as it compares an effect (e.g. difference in group means) to the variability of the sample. The variability is inevitably larger if a lot of noisy, artifactual, and quite likely erroneous data are included. While some degree of this can be accounted for in meta-analysis by using a random-effects model, it simply doesn’t make sense to include bad data. We are not interested in the meta-effect, that is, the average result over all possible experimental designs we can dream up, no matter how inadequate.
What we are actually interested in is some biological effect and we should ensure that we take the most precise measurement as possible. Once you have a procedure that you are confident will yield precise measurements, by all means, carry out a confirmatory experiment. Replicate it several times, especially if it’s not an obvious effect. Pre-register your design if you feel you should. Maximise statistical power by testing many subjects if necessary (although often significance is tested on a subject-by-subject basis, so massive sample sizes are really overkill as you can treat each participant as a replication – I’ll talk about replication in a future post so I’ll leave it at this for now). But before you do all this you usually have to fine-tune an experiment, at least if it is a novel problem.
Isn’t this contributing to the problem?
Colleagues in social/personality psychology often seem to be puzzled and even concerned by this. The opacity of what has or hasn’t been tried is part of the problems that plague the field and lead to publication bias. There is now a whole industry meta-analysing results in the literature to quantify ‘excess significance’ or a ‘replication index’. This aims to reveal whether some additional results, especially null results, may have been suppressed or if p-hacking was employed. Don’t these pilot experiments count as suppressed studies or p-hacking?
No, at least not if this is done properly. The criteria you use to design your study must of course be orthogonal to and independent from your hypothesis. Publication bias, p-hacking, and other questionable practices are all actually sub-forms of circular reasoning: You must never use the results of your experiment to inform the design as you may end up chasing (overfitting) ghosts in your data. Of course, you must not run 2-3 subjects on an experiment, look at the results and say ‘The hypothesis wasn’t confirmed. Let’s tweak a parameter and start over.’ This would indeed be p-hacking (or rather ‘result hacking’ – there are usually no p-values at this stage).
A real example
I can mainly speak from my own experience but typically the criteria used to set up psychophysics experiments are sanity/quality checks. Look for example at the figure below, which shows a psychometric curve of one participant. The experiment was a 2AFC task using the method of constant stimuli: In each trial the participant made a perceptual judgement on two stimuli, one of which (the ‘test’) could vary physically while the other remained constant (the ‘reference’). The x-axis plots how different the two stimuli were, so 0 (the dashed grey vertical line) means they were identical. To the left or right of this line the correct choice would be the reference or test stimulus, respectively. The y-axis plots the percentage of trials the participant chose the test stimulus. By fitting a curve to these data we can extrapolate the ability of the participant to tell apart the stimuli – quantified by how steep the curve is – and also their bias, that is at what level of x the two stimuli appeared identical to them (dotted red vertical line):
As you can tell, this subject was quite proficient at discriminating the stimuli because the curve is rather steep. At many stimulus levels the performance is close to perfect (that is, either near 0 or 100%). There is a point where performance is at chance (dashed grey horizontal line). But once you move to the left or the right of this point performance becomes good very fast. The curve is however also shifted considerably to the right of zero, indicating that the participant indeed had a perceptual bias. We quantify this horizontal shift to infer the bias. This does not necessarily tell us the source of this bias (there is a lot of literature dealing with that question) but that’s beside the point – it clearly measures something reliably. Now look at this psychometric curve instead:
The general conventions here are the same but these results are from a completely different experiment that clearly had problems. This participant did not make correct choices very often as the curve only barely goes below the chance line – they chose the test stimulus far too often. There could be numerous reasons for this. Maybe they didn’t pay attention and simply made the same choice most of the time. For that the trend is bit too clean though. Perhaps the task was too hard for them, maybe because the stimulus presentation was too brief. This is possible although it is very unlikely that a healthy, young adult with normal vision would not be able to tell apart the more extreme stimulus levels with high accuracy. Most likely, the participant did not really understand the task instructions or perhaps the stimuli created some unforeseen effect (like the illusion I mentioned before) that actually altered what percept they were judging. Whatever the reason, there is no correct way to extrapolate the psychometric parameters here. The horizontal shift and the slope are completely unusable. We see an implausibly poor discrimination performance and extremely large perceptual bias. If their vision really worked this way, they should be severely impaired…
So these data are garbage. It makes no sense to meta-analyse biologically implausible parameter estimates. We have no idea what the participant was doing here and thus we can also have no idea what effect we are measuring. Now this particular example is actually a participant a student ran as part of their project. If you did this pilot experiment on yourself (or a colleague) you might have worked out what the reason for the poor performance was.
What can we do about it?
In my view, it is entirely justified to exclude such data from our publicly shared data repositories. It would be a major hassle to document all these iterations. And what is worse, it would obfuscate the results for anyone looking at the archive. If I look at a data set and see a whole string of brief attempts from a handful of subjects (usually just the main author), I could be forgiven for thinking that something dubious is going on here. However, in most cases this would be unjustified and a complete waste of everybody’s time.
At the same time, however, I also believe in transparency. Unfortunately, some people do engage in result-hacking and iteratively enhance their findings by making the experimental design contingent on the results. In most such cases this is probably not done deliberately and with malicious intent – but that doesn’t make it any less questionable. All too often people like to fiddle with their experimental design while the actual data collection is already underway. In my experience this tendency is particularly severe among psychophysicists who moved into neuroimaging where this is a really terrible (and costly) idea.
How can we reconcile these issues? In my mind, the best way is perhaps to document briefly what you did to refine the experimental design. We honestly don’t need or want to see all the failed attempts at setting up an experiment but it could certainly be useful to have an account of how the design was chosen. What experimental parameters were varied? How and why were they chosen? How many pilot participants were there? This last point is particularly telling. When I pilot something, there usually is one subject: Sam. Possibly I will have also tested one or two others, usually lab members, to see if my familiarity with the design influences my results. Only if the design passes quality assurance, say by producing clear psychometric curves or by showing to-be-expected results in a sanity check (e.g., the expected response on catch trials), I would dare to actually subject “real” people to a novel design. Having some record, even if as part of the documentation of your data set, is certainly a good idea though.
The number of participants and pilot experiments can also help you judge the quality of the design. Such “fine-tuning” and tweaking of parameters isn’t always necessary – in fact most designs we use are actually straight-up replications of previous ones (perhaps with an added condition). I would say though that in my field this is a very normal thing to do when setting up a new design at least. However, I have also heard of extreme cases that I find fishy. (I will spare you the details and will refrain from naming anyone). For example in one study the experimenters ran over a 100 pilot participants – tweaking the design all along the way – to identify those that showed a particular perceptual effect and then used literally a handful of these for an fMRI study that claims to have been about “normal” human brain function. Clearly, this isn’t alright. But this also cannot possibly count as piloting anymore. The way I see it, a pilot experiment can’t have an order of magnitude more data than the actual experiment…
How does this relate to the wider debate?
I don’t know how applicable these points are to social psychology research. I am not a social psychologist and my main knowledge about their experiments are from reading particularly controversial studies or the discussions about them on social media. I guess that some of these issues do apply but that it is far less common. An equivalent situation to what I describe here would be that you redesign your questionnaire because it people always score at maximum – and by ‘people’ I mean the lead author :P. I don’t think this is a realistic situation in social psychology, but it is exactly how psychophysical experiments work. Basically, what we do in piloting is what a chemist would do when they are calibrating their scales or cleaning their test tubes.
Or here’s another analogy using a famous controversial social psychology finding we discussed previously: Assume you want to test whether some stimulus makes people walk more slowly as they leave the lab. What I do in my pilot experiments is to ensure that the measurement I take of their walking speed is robust. This could involve measuring the walking time for a number of people before actually doing any experiment. It could also involve setting up sensors to automate this measurement (more automation is always good to remove human bias but of course this procedure needs to be tested too!). I assume – or I certainly hope so at least – that the authors of these social psychology studies did such pre-experiment testing that was not reported in their publications.
As I said before, humans are dirty test tubes. But you should ensure that you get them as clean as you can before you pour in your hypothesis. Perhaps a lot of this falls under methods we don’t report. I’m all for reducing this. Methods sections frequently lack necessary detail. But to some extend, I think some unreported methods and tests are unavoidable.
Yesterday Neuroskeptic came to our Cognitive Drinks event in the Experimental Psychology department at UCL to talk about p-hacking. His entertaining talk (see Figure 1) was followed by a lively and fairly long debate about p-hacking and related questions about reproducibility, preregistration, and publication bias. During the course of this discussion a few interesting things came up. (I deliberately won’t name anyone as I think this complicates matters. People can comment and identify themselves if they feel that they should…)
It was suggested that a lot of the problems with science would be remedied effectively if only people were encouraged (or required?) to replicate their own findings before publication. Now that sounds generally like a good idea. I have previously suggested that this would work very well in combination with preregistration: you first do a (semi-)exploratory experiment to finalise the protocol, then submit a preregistration of your hypothesis and methods, and then do the whole thing again as a replication (or perhaps more than one if you want to test several boundary conditions or parameters). You then submit the final set of results for publication. Under the Registered Report format, your preregistered protocol would already undergo peer review. This would ensure that the final results are almost certain to be published provided you didn’t stray excessively from the preregistered design. So far, so good.
Should you publish unclear results?
Or is it? Someone suggested that it would be a problem if your self-replication didn’t show the same thing as the original experiment. What should one do in this case? Doesn’t publishing something incoherent like this, one significant finding and a failed replication, just add to the noise in the literature?
At first, this question simply baffled me, as I suspect it would many of the folks campaigning to improve science. (My evil twin sister called these people Crusaders for True Science but I’m not supposed to use derogatory terms like that anymore nor should I impersonate lady demons for that matter. Most people from both sides of this mudslinging contest “debate” never seemed to understand that I’m also a revolutionary – you might just say that I’m more Proudhon, Bakunin, or Henry David Thoreau rather than Marx, Lenin, or Che Guevara. But I digress…)
Surely, the attitude that unclear, incoherent findings, that is, those that are more likely to be null results, are not worth publishing must contribute to the prevailing publication bias in the scientific literature? Surely, this view is counterproductive to the aims of science to accumulate evidence and gradually get closer to some universal truths? We must know which hypotheses have been supported by experimental data and which haven’t. One of the most important lessons I learned from one of my long-term mentors was that all good experiments should be published regardless of what they show. This doesn’t mean you should publish every single pilot experiment you ever did that didn’t work. (We can talk about what that does and doesn’t mean another time. But you know how life is: sometimes you think you have some great idea only to realise that it makes no sense at all when you actually try it in practice. Or maybe that’s just me? :P). Even with completed experiments you probably shouldn’t bother publishing if you realise afterwards that it is all artifactual or the result of some error. Hopefully you don’t have a lot of data sets like that though. So provided you did an experiment of suitable quality I believe you should publish it rather than hiding it in the proverbial file drawer. All scientific knowledge should be part of the scientific record.
I naively assumed that this view was self-evident and shared by almost everyone – but this clearly is not the case. Yet instead of sneering at such alternative opinions I believe we should understand why people hold them. There are reasonable arguments why one might wish to not publish every unclear finding. The person making this suggestion at our discussion said that it is difficult to interpret a null result, especially an assumed null result like this. If your original experiment O showed a significant effect supporting your hypothesis, but your replication experiment R does not, you cannot naturally conclude that the effect really doesn’t exist. For one thing you need to be more specific than that. If O showed a significant positive effect but R shows a significant negative one, this would be more consistent with the null hypothesis than if O is highly significant (p<10-30) and R just barely misses the threshold (p=0.051).
So let’s assume that we are talking about the former scenario. Even then things aren’t as straightforward, especially if R isn’t as exact a replication of O as you might have liked. If there is any doubt (and usually there is) that something could have been different in R than in O, this could be one of the hidden factors people always like to talk about in these discussions. Now you hopefully know your data better than anyone. If experiment O was largely exploratory and you tried various things to see what works best (dare we say p-hacking again?), then the odds are probably quite good that a significant non-replication in the opposite direction shows that the effect was just a fluke. But this is not a natural law but a probabilistic one. Youcannot everknow whether the original effect was real or not, especially not from such a limited data set of two non-independent experiments.
This is precisely why you should publish all results!
In my view, it is inherently dangerous if researchers decide for themselves which findings are important and which are not. It is not only a question of publishing only significant results. It applies much more broadly to the situation when a researcher publishes only results that support their pet theory but ignores or hides those that do not. I’d like to believe that most scientists don’t engage in this sort of behaviour – but sadly it is probably not uncommon. A way to counteract this is to train researchers to think of ways that test alternative hypotheses that make opposite predictions. However, such so-called “strong inference” is not always feasible. And even when it is, the two alternatives are not always equally interesting, which in turn means that people may still become emotionally attached to one hypothesis.
The decision whether a result is meaningful should be left to posterity. You should publish all your properly conducted experiments. If you have defensible doubts that the data are actually rubbish (say, an fMRI data set littered with spikes, distortions, and excessive motion artifacts, or a social psychology study where you discovered posthoc that all the participants were illiterate and couldn’t read the questionnaires) then by all means throw them in the bin. But unless you have a good reason, you should never do this and instead add the results to the scientific record.
Now the suggestion during our debate was that such inconclusive findings clog up the record with unnecessary noise. There is an enormous and constantly growing scientific literature. As it is, it is becoming increasingly harder to separate the wheat from the chaff. I can barely keep up with the continuous feed of new publications in my field and I am missing a lot. Total information overload. So from that point of view the notion makes sense that only those studies that meet a certain threshold for being conclusive are accepted as part of the scientific record.
I can certainly relate to this fear. For the same reason I am sceptical of proposals that papers should be published before review and all decisions about the quality and interest of some piece of research, including the whole peer review process, should be entirely post-publication. Some people even seem to think that the line between scientific publication and science blog should be blurred beyond recognition. I don’t agree with this. I don’t think that rating systems like those used on Amazon or IMDb are an ideal way to evaluate scientific research. It doesn’t sound wise to me to assess scientific discoveries and medical breakthroughs in the same way we rank our entertainment and retail products. And that is not even talking about unleashing the horror of internet comment sections onto peer review…
Solving the (false) dilemma
I think this discussion is creating a false dichotomy. These are not mutually exclusive options. The solution to a low signal-to-noise ratio in the scientific literature is not to maintain publication bias of significant results. Rather the solution is to improve our filtering mechanisms. As I just described, I don’t think it will be sufficient to employ online shopping and social network procedures to rank the scientific literature. Even in the best-case scenario this is likely to highlight the results of authors who are socially dominant or popular and probably also those who are particularly unpopular or controversial. It does not necessarily imply that the highest quality research floats to the top [cue obvious joke about what kind of things float to the top…].
No, a high quality filter requires some organisation. I am convinced the scientific community can organise itself very well to create these mechanisms without too much outside influence. (I told you I’m Thoreau and Proudhon, not some insane Chaos Worshipper :P). We need some form of acceptance to the record. As I outlined previously, we should reorganise the entire publication process so that the whole peer-review process is transparent and public. It should be completely separate from journals. The journals’ only job should be to select interesting manuscripts and to publish short summary versions of them in order to communicate particularly exciting results to the broader community. But this peer-review should still involve a “pre-publication” stage – in the sense that the initial manuscript should not generate an enormous amount of undue interest before it has been properly vetted. To reiterate (because people always misunderstand that): the “vetting” should be completely public. Everyone should be able to see all the reviews, all the editorial decisions, and the whole evolution of the manuscript. If anyone has any particular insight to share about the study, by all means they should be free to do so. But there should be some editorial process. Someone should chase potential reviewers to ensure the process takes off at all.
The good news about all this is that it benefits you. Instead of weeping bitterly and considering to quit science because yet again you didn’t find the result you hypothesised, this just means that you get to publish more research. Taking the focus off novel, controversial, special, cool or otherwise “important” results should also help make the peer review more about the quality and meticulousness of the methods. Peer review should be about ensuring that the science is sound. In current practice it instead often resembles a battle with authors defending to the death their claims about the significance of their findings against the reviewers’ scepticism. Scepticism is important in science but this kind of scepticism is completely unnecessary when people are not incentivised to overstate the importance of their results.
Practice what you preach
I honestly haven’t followed all of the suggestions I make here. Neither have many other people who talk about improving science. I know of vocal proponents of preregistration who have yet to preregister any study of their own. The reasons for this are complex. Of course, you should “be the change you wish to see in the world” (I’m told Gandhi said this). But it’s not always that simple.
On the whole though I think I have published almost all of the research I’ve done. While I currently have a lot of unpublished results there is very little in the file drawer as most of these experiments have either been submitted or are being written up for eventual publication. There are two exceptions. One is a student project that produced somewhat inconclusive results although I would say it is a conceptual replication of a published study by others. The main reason we haven’t tried to publish this yet is that the student isn’t here anymore and hasn’t been in contact and the data aren’t that exciting to us to bother with the hassle of publication (and it is a hassle!).
The other data set is perhaps ironic because it is a perfect example of the scenario I described earlier. A few years ago when I started a new postdoc I was asked to replicate an experiment a previous lab member had done. For simplicity, let’s just call this colleague Dr Toffee. Again, they can identify themselves if they wish. The main reason for this was that reviewers had asked Dr Toffee to collect eye-movement data. So I replicated the original experiment but added eye-tracking. My replication wasn’t an exact one in the strictest terms because I decided to code the experimental protocol from scratch (this was a lot easier). I also had to use a different stimulus setup than the previous experiment as that wouldn’t have worked with the eye-tracker. Still, I did my best to match the conditions in all other ways.
My results were a highly significant effect in the opposite direction than the original finding. We did all the necessary checks to ensure that this wasn’t just a coding error etc. It seemed to be real. Dr Toffee and I discussed what to do about it and we eventually decided that we wouldn’t bother to publish this set of experiments. The original experiment had been conducted several years before my replication. Dr Toffee had moved on with their life. I on the other hand had done this experiment as a courtesy because I was asked to. It was very peripheral to my own research interests. So, as in the other example, we both felt that going through the publication process would have been a fairly big hassle for very little gain.
Now this is bad. Perhaps there is some other poor researcher, a student perhaps, who will do a similar experiment again and waste a lot of time on testing the hypothesis that, at least according to our incoherent results, is unlikely to be true. And perhaps they will also not publish their failure to support this hypothesis. The circle of null results continues…
But you need to pick your battles. We are all just human beings and we do not have unlimited (research) energy. With both of these lacklustre or incoherent results I mentioned (and these are literally the only completed experiments we haven’t at least begun to write up), it seems like a daunting task to undergo the pain of submission->review->rejection->repeat that simply doesn’t seem worth it.
So what to do? Well, the solution is again what I described. The very reason the task of publishing these results isn’t worth our energy is everything that is wrong with the current publication process! In my dream world in which I can simply write up a manuscript formatted in a way that pleases me and then upload this to the pre-print peer-review site my life would be infinitely simpler. No more perusing dense journal websites for their guide to authors or hunting for the Zotero/Endnote/Whatever style to format the bibliography. No more submitting your files to one horribly designed, clunky journal website after another, checking the same stupid tick boxes, adding the same reviewer suggestions. No more rewriting your cover letters by changing the name of the journal. Certainly for my student’s project, it would not be hard to do as there is already a dissertation that can be used as a basis for the manuscript. Dr Toffee’s experiment and its contradictory replication might require a bit more work – but to be fair even there is already a previous manuscript. So all we’d need to add would be the modifications of the methods and the results of my replication. In a world where all you need to do is upload the manuscript and address some reviewers’ comments to ensure the quality of the science this should be fairly little effort. In turn it would ensure that the file drawer is empty and we are all much more productive.
This world isn’t here yet but there are journals that will allow something that isn’t too far off from that, namely F1000Research and PeerJ (and the Winnower also counts although the content there seems to be different and I don’t quite know how much review editing happens there). So, maybe I should email Dr Toffee now…
(* In case you didn’t get this from the previous 2700ish words: the answer to this question is unequivocally “No.”)
Recently I have been thinking a bit about what the best way is to represent group data. The most typical way this is done is by showing summary statistics (usually the mean) and error bars (usually standard errors) either in bar plots or in plots with lines and symbols. A lot of people seem to think this is not an appropriate way to visualise results because it obscures the data distribution and also whether outliers may influence the results. One reason prompting me to think about this is that in at least one of our MSc courses students are explicitly told by course tutors that they should be plotting individual subject data. It is certainly true that close inspection of your data is always important – but I am not convinced that it is the only and best way to represent all sorts of data. In particular, looking at the results from an experiment of a recent student of mine you wouldn’t make heads or tails from just plotting individual data. Part of the reason is that most of the studies we do use within-subject designs and standard ways of plotting individual data points can actually be misleading. There are probably better ones, and perhaps my next post will deal with that.
For now though I want to only consider group data which were actually derived from between-subject or at least mixed designs. A recently published study in Psychological Science reported that sad people are worse at discriminating colours along the blue-yellow colour axis but not along the red-green colour axis. This sparked a lot of discussion on Twitter and in the blogosphere, for example this post by Andrew Gelman and also this one by Daniel Lakeland. Publications like this tend to attract a lot of coverage by mainstream media and this was no exception. This then further fuels the rage of skeptical researchers :P. There are a lot of things to debate here, from the fact that the study authors interpret a difference between differences as significant without testing the interaction, the potential inadequacy of the general procedure for measuring perceptual differences (raw accuracy rather than a visual threshold measure), and also that outliers may contribute to the main result. I won’t go into this discussion but I thought this data set (which to the authors’ credit is publicly available) would be a good example for my musings.
So here I am representing the data from their first study by plotting it in four different ways. The first plot, in the upper left, is a bar plot showing the means and standard errors for the different experimental conditions. The main result in the article is that the difference between control and sadness is significant for discriminating colours along the blue-yellow axis (the two bars on the left).
And judging by the bar graph you could certainly be forgiven for thinking so (I am using the same truncated scale used in the original article). The error bars seem reasonably well separated and this comparison is in fact statistically significant at p=0.0147 on a parametric independent sample t-test or p=0.0096 on a Mann-Whitney U-test (let’s ignore the issue of the interaction for this example).
Now consider the plot in the upper right though. Here we have the individual data points for the different groups and conditions. To give an impression of how the data are distributed, I added a little Gaussian noise to the x-position of each point. The data are evidently quite discrete due to the relatively small number of trials used to calculate the accuracy for every subject. Looking at the data in this way does not seem to give a very clear impression that there is a substantial difference between the control and sadness groups in either colour condition. The most noticeable difference is that there is one subject in the sadness group whose accuracy is not matched with any counterpart in the control group, at 0.58 accuracy. Is this an outlier pulling the result?
Next I generated a box-and-whisker plot in the lower left panel. The boxes in these plots denote the inter-quartile range (IQR, i.e. between 25th and 75th percentile of the data), the red lines indicate the medians, the error bars denote a range of 1.5 times the IQR beyond the percentiles (although it is curtailed when there are no data points beyond that range as by the ceiling at 1), and the red crosses are outliers that fall outside this range. The triangular notches surrounding the medians are a way to represent uncertainty and if they do not overlap (as is the case for the blue-yellow data) this suggests a difference between medians at the 5% significance level. Clearly the data point at 0.58 accuracy in the sadness group is considered an outlier in this plot although it is not the only one.
Finally, I also wrote a Matlab function to create cat-eye plots (Wikipedia calls those violin plots – personally they look mostly like bottles, amphoras or vases to me – or, in this case, like balloons). This is shown in the lower right panel. These plots show the distribution of the data in each condition smoothed by a kernel density function. The filled circles indicate the median, the vertical lines the inter-quartile range, and the asterisk the mean. Plots like this seem to be becoming more popular lately. They do have the nice feature that they give a fairly direct impression of how the data are distributed. It seems fairly clear that these are not normal distributions, which probably has largely to do with the ceiling effect: as accuracy cannot be higher than 1 the distributions are truncated there. The critical data set, the blue-yellow discrimination for the sadness group, has a fairly thick tail towards the bottom which is at least partially due to that outlier. This all suggests that the traditional t-test was inappropriate here but then again we did see a significant difference on the U-test. And certainly, visual inspection still suggests that there may be a difference here.
Next I decided to see what happens if I remove this outlier at 0.58. For consistency, I also removed their data from the red-green data set. This change does not alter the statistical inference in a qualitative way even though the p-values increase slightly. The t-test is still significant at p=0.0259 and the U-test at p=0.014.
Again, the bar graph shows a fairly noticeable difference. The scatter plot of the individual data points on the other hand now hardly seems to show any difference. Both the whisker and the cat-eye plot seem to still show qualitatively similar results as when the outlier is included. There seems to be a difference in medians for the blue-yellow data set. The cat-eye plot makes is more apparent that the tail of the distribution for the sadness group is quite heavy something that isn’t that clear in the whisker plot.
Finally, I decided to simulate a new data set with a similar pattern of results but in which I knew the ground truth. All four data sets contained 50 data points that were chosen from a Gaussian distribution with mean of 70 and standard deviation of 10 (I am a moron and therefore generated these on a scale of percent rather than proportion correct – and now I’m too lazy to replot all this just to correct it. It doesn’t matter really). For the control group in the blue-yellow condition I added an offset of 5 while in the sadness group I subtracted 5. This means that there is a significant difference (t-test: p=0.0017; U-test: 0.0042).
Now all four types of plot fairly clearly reflect this difference between control and sadness groups. The bar graph in particular clearly reflects the true population means in each group. But even in the scatter plot the difference is clearly apparent even though the distributions overlap considerably. The difference seems a lot less obvious in the whisker and cat-eye plots however. The notches in the whisker plot do not overlap although they seem to be very close. The difference seems to be more visually striking for the cat-eye plot but it isn’t immediately apparent from the plot how much confidence this should instill in this result.
Conclusions & Confusions
My preliminary conclusion is that all of this is actually more confusing than I thought. I am inclined to agree that the bar graph (or a similar symbol and error bar plot) seems to overstate the strength of the evidence somewhat (although one should note that this is partly because of the truncated y-scales that such plots usually employ). On the other hand, showing the individual subject data does seem to understate the results considerably except when the effect is pretty strong. So perhaps things like whisker or cat-eye (violin/bottle/balloon) plots are the most suitable but in my view they also aren’t as intuitive as some people seem to suggest. Obviously, I am not the first person who has thought about these things nor have I spent an extraordinarily long time thinking about it. It might be useful to conduct a experiment/survey in which people have to judge the strength of effects based on different kinds of plot. Anyway, in general I would be very curious to hear other people’s thoughts.
The Matlab code and data file for these examples can be found here.
Because it’s so much more fun than the things I should really be doing (correcting student dissertations and responding to grant reviews) I read a long blog post entitled “Science isn’t broken” by Christie Aschwanden. In large parts this is a summary of the various controversies and “crises” that seem to have engulfed scientific research in recent years. The title is a direct response to an event I participated in recently at UCL. More importantly, I think it’s a really good read so I recommend it.
This post is a quick follow-up response to the general points raised there. As I tried to argue (probably not very coherently) at that event, I also don’t think science is broken. First of all, probably nobody seriously believes that the lofty concept of science, the scientific method (if there is one such thing), can even be broken. But even in more pragmatic terms, the human aspects of how science works are not broken either. My main point was that the very fact we are having these kinds of discussions, about how scientific research can be improved, is direct proof that science is in fact very healthy. This is what self-correction looks like.
If anything, the fact that there has been a recent surge of these kinds of debates shows that science has already improved a lot recently. After decades of complacency with the status quo there now seems to be real energy afoot to effect some changes. However, it is not the first time this happened (for example, the introduction of peer review would have been a similarly revolutionary time) and it will not be the last. Science will always need to be improved. If some day conventional wisdom were that our procedure is now perfect, that it cannot be improved anymore, that would be a tell-tale sign for me that I should do something else.
So instead of fretting over whether science is “broken” (No, it isn’t) or even whether it needs improvement (Yes, it does), what we should be talking about is specifically what really urgently needs improvement. Here is my short list. I am not proposing many solutions (except for point 1). I’d be happy to hear suggestions:
I. Publishing and peer review
The way we publish and review seriously needs to change. We are wasting far too much time on trivialities instead of the science. The trivialities range from reformatting manuscripts to fit journal guidelines and uploading files on the practical side to chasing impact factors and “novel” research on the more abstract side. Both hurt research productivity although in different ways. I recently proposed a solution that combines some of the ideas by Dorothy Bishop and Micah Allen (and no doubt many others).
II. Post-publication review
Related to this, the way we evaluate and discuss published science needs to change, too. We need to encourage more post-publication review. This currently still doesn’t happen as most studies never receive any post-pub review or get commented on at all. Sure, some (including some of my own) probably just don’t deserve any attention, but how will you know unless somebody tells you the study even exists? Many precious gems will be missed that way. This has of course always been the case in science but we should try to minimise that problem. Some believe post-publication review is all we will ever need but unless there are robust mechanisms to attract reviewers to new manuscripts besides the authors’ fame, (un-)popularity, and/or their social media presence – none of which are good scientific arguments – I can’t see how a post-pub only system can change this. On this note I should mention that Tal Yarkoni, with whom I’ve had some discussions about this issue, wrote an article about this which presents some suggestions. I am not entirely convinced of the arguments he makes for enhancing post-publication review but I need more time to respond to this in detail. So I will just point this out for now to any interested reader.
III. Research funding and hiring decisions
Above all, what seriously needs to change is how we allocate research funds and how we make hiring decisions. The solution to that probably goes hand in hand with solving the other two points, but I think it also requires direct action now in the absence of good solutions for the other issues. We must stop judging grant and job applicants based on impact factors or h-indeces. This is certainly more easily done for job applications than for grant decisions as in the latter the volume of applications is much greater – and the expertise of the panel members in judging the applications is lower. But it should be possible to reduce the reliance on metrics and ratings – even newer, more refined ones. Also grant applications shouldn’t be killed by a single off-hand critical review comment. Most importantly, grants shouldn’t all be written in a way that devalues exploratory research (by pretending to have strong hypotheses when you don’t) or – even worse – by pretending that the research you already conducted and are ready to publish is a “preliminary pilot data set.” For work that actually is hypothesis driven I quite like Dorothy Bishop’s idea that research funds could be obtained at the pre-registration stage when the theoretical background and experimental design have been established but before data collection commences. Realistically, this is probably more suitable for larger experimental programs than for every single study. But then again, encouraging larger, more thorough, projects may in fact be a good thing.