As the attentive reader of this blog might have noticed, I don’t post much any more. We now live in a world where NeuroSkeptic of all people has also stopped blogging. As he rightly says, the internet isn’t really the same as it was, and this isn’t really the best medium for communicating anymore. I also simply neither have the time, energy, or – frankly – the desire to write here either.
Therefore, I can no longer justify maintaining this site and I’m closing the final page on this blog. The domain is set to expire within days (probably takes a while to effect). After this, the posts should remain visible for posterity. Thanks to everyone who read my posts and interesting discussions here and elsewhere.
You know where to find me… (i.e. not on Twitter – I hardly go there anymore even when we’re not Level 4 lockdown 😉
After watching – and briefly being at the receiving end of – the latest bullshit tsunami about the Covid vaccines, I’ve decided to write another blog post1 about scepticism and the value of scientific expertise. And then I realised I had already written that post a year ago :P. That’s great – it saves me time that I don’t really have in the first place! So instead I decided to list a few heuristics in the style of Occam’s Razor. While I have slim hope, perhaps they will help in fighting the bullshit in which we are drowning.
Snopes Razor: When your racist relative/former highschool classmate/contrarian ex-colleague posts something on Facebook, there is probably already a Snopes.com article debunking it.
Soros Razor: If they say that fact-checkers like Snopes or the BBC cannot be trusted because “they are in the pocket of George Soros/Bill Gates/Satanists/Aliens/Jewish Space Lasers”, don’t waste your breath and block them at once.
360 Razor: Whenever the bullshitter pleads with you to “look at all the evidence from every angle”, they usually want you to look only at their evidence from their angle.
Majority Razor: When 9 out of 10 experts agree that something is bullshit, it probably is.2
NOFX Razor: Then again, just because everyone in your bubble believes the bullshit doesn’t make it right.3
Expert Razor: The bullshitter’s “scientific expert” has a PhD but it’s in a field that has nothing to do with the topic in question and/or their professorship is at a non-existent university.
Read-on Razor: If the bullshitter posts the title of a scientific article to make their point, read the abstract. If they post the abstract, read the whole article. It will inevitably say the exact opposite to what the bullshitter claims it does.
Extrapolation Razor: The bullshitter’s main thesis is inevitably based on a pretty wild misconstrual or outright deliberate distortion of something someone said or did in good faith.4
Oversimplification Razor: The bullshitter’s understanding of scientific evidence will not only be limited but overly simplistic without room for relative evidence or nuance.5
The Rabbit Hole: If a bullshitter bullshits about one bullshit they inevitably bullshit about other bullshit, too. And the bullshitting will only get worse. Bullshit begets bullshit.
1) How obvious is it that I’m getting as much of this out of my system before I let the domain expire and retire from blogging for good…?
2) It’s true, a single brilliant insight can revolutionise our understanding. But Galileo did that because he was right, not because he defied the establishment. The truth will out eventually. And on this note:
4) For a first-hand demonstration of this phenomenon, google “Bill Gates vaccine population control”. Then after reading for a bit you’ll want to take a good shower to scrub off that icky feeling. (If you’re in Auckland, keep it under 4 minutes though – it may be under some control now but we still have a water shortage…)
5) The interpretation of data is also highly asymmetric. To the bullshitter, 95% efficacy means “ineffective” while 0.00001% constitutes a “mortal risk”. That’s for example why “Vaccines don’t stop transmission”. The reason you don’t know anyone who died of smallpox or polio is sunspots. Incidentally, sunspots are also to blame for climate change of course. Except for the climate change that escaped from a Chinese climate lab.
Here is another post on experimental design and data analyses. I need to get this stuff out of my system before I’m letting the domain on this blog expire at the end of the year (I had planned this for last year already but then decided to keep it going because of a certain difficult post I must write then…)
Hidden group differences?
This (hopefully brief) post is inspired by a Twitter discussion I had last night. These people have had a journal club about one of my lab ‘s recent publications. The details of that are not really important for this post – you can read their excellent questions about our work and my replies to them in the tweet thread. However, what this discussion reminded me of is the issues you can run into when dealing with human volunteer participants that you have no control over and – what is worse – you may not even be aware of.
In this particular study, we compared retinotopic maps from groups of identical (MZ) and fraternal (DZ) twin pairs. One very notable point when you read our article is that the sample sizes for the two groups are quite different, with more MZ twin pairs than DZ pairs. We had some major difficulties finding DZ twins to take part and what made matters worse is that we had to reclassify several purported DZ twins to MZ twins after genetic testing. Looking at the literature, this seems quite common. For example, we found that in the Human Connectome Project there is a similar imbalance in the sample sizes (see for instance this preprint that also looked at retinotopic maps in twins at a more macroscopic level). A colleague of ours working on another twin study experienced the same problem (I don’t think this study has been published yet). Finally, here is just one more example of a vision science study with substantially greater sample for MZ than DZ twins.
There are clearly problems recruiting DZ twins. Undoubtedly MZ twins are more “special”, and so there are organisations through which they can be reached. While there are participant pools for twins that contain both zygosities, the people managing these can be rather protective. This is understandable because these databases are a valuable scientific resource and they don’t want to tire out their participants by allowing too many researchers to approach them with requests to participate. These pools of participants may also be imbalanced because MZ self-select into them because they have a strong interest to learn about how similar they are. In contrast, DZ twins may have less interest in this question (although some obviously do). And even if you have a well-balanced pool of potential participants, there may be additional social factors at play. The MZ twins in those pools may be keener to take part than the DZ twins. Of course, the zygosity may also interact in hidden ways with this. MZ twins might have a closer relationship to one another, even if just being more geographically closer, and that will doubtless affect how easy it is for them to participate in your study. All these issues are extremely difficult to know about, let alone to control.
Not about twins
As I said, the details of our study aren’t really important and this post isn’t about twins. Rather, this is clearly a broader issue. Similar concerns affect any comparison between groups of participants. Anyone studying patients with a particular condition is probably familiar with that issue. Many patients are keen to take part in studies because they have an interest in better understanding their condition or – for some disorders or illnesses – contributing to the development of treatments. In contrast, recruiting the “matched” control participants can be very difficult and you may go to great and unusual lengths to find them. This can result in your control group being quite unusual compared to the standard participant sample you might have when you do fundamental research, especially considering a lot of such research is done on young undergraduate students recruited on university campuses.
Let’s imagine for example that we want to understand visual processing by professional basketball players in the NBA. A quick Googling suggests the average body height of NBA players is 1.98 m, considerably taller than the average male. Any comparison that does not take this into account would confound body height with basketball skill. Obviously you can control aspects like this to some extent by using covariates (e.g. in multiple regression analyses) – but that is only for the variables you know about. More importantly, you’d be well-advised to recruit a matched control group that has similar body height as your basketball players but without the athletic skills. That way you cancel out the effect of body height.
But how does this recruitment drive interact with your samples? For one thing, it will probably be difficult to find these tall controls. While most NBA players are very tall (even short NBA players are presumably above average height), really tall people in the general population are rare. So finding them may take a long time. But what is worse, the ones you do find may also differ in other respects from your average person. For body height, this may not be too problematic but you never know what issues a very tall person faces who doesn’t happen to have a multi-million dollar athletic contract.
These issues can be quite nefarious. For instance, I was involved in a study a few years ago where we must recruit control participants matched to our main group of interest both in terms of demographic details and psychological measures. What we ended up with was a lot of exclusions of potential control partipants due to drug use, tattoos or metal implants (a safety hazard), and in one case an undisclosed medical history we only discovered serendipitously. The rationale for selecting participants with particular matched traits from the general population is based on the assumption that these traits are random – however, this fails if there is some hidden association between that trait and other confounding factors. In essence, this is just another form of selection bias that I have written about recently…
The problem is there is simply no good way to control for that. You cannot use a variable as covariate when you don’t know it exists. This means that particular variable simply becomes part of the noise, the variance not explained by your model. It is entirely possible that this noise masquerades as a difference that doesn’t really exist (Type I error) or obscures true effects (Type II error). You can and should obviously check for potential caveats and thus establish the robustness of the findings but that can only go so far.
Small N designs
This brings me back to another one of my pet issues: small N designs, as are common in psychophysics. Some psychophysics experiments have as few as two participants, both of whom are also authors of the publication. It is debatable how valid this extreme might be – one of my personal heuristics is that you should always include some “naive” observers (or at least one?) to show that results do not crucially depend on knowledge of the hypothesis. But these designs can nevertheless be valid. Many experiments are actually difficult for the participant to influence through mere willpower alone. I’ve done some experiments on myself where I thought I was responding a certain way only to find the results didn’t reflect this intuition at all.
And there is definitely something to be said about having trained observers. I’ve covered this topic several times before so I won’t go in detail on this. But it doesn’t really make sense to contaminate your results with bad data. A lot of psychophysical experiments require steady eye gaze to ensure that stimuli are presented at the parafoveal and peripheral locations you want to test. It doesn’t make much sense to include participants who cannot maintain fixation. (On that note, it is interesting that some results can actually be surprisingly robust even in the presence of considerable eye movements – such as what we found in this study. This opens up a number of questions as to what those results mean but I have not yet figured out a good way to answer them…).
This is quite different from your typical psychology experiment. Imagine you want to test (bear with me here) how fast your participants walk down the corridor after leaving your lab cubicle where you had them do some task with words… While there may be some justified reasons for exclusion of participants (such as that they obviously didn’t comply with your task instructions or failed to understand the words or that they get an urgent phone call that caused them to sprint down the hall), there is no such thing as a “trained observer” here. You want to make an inference about how the average person reacts to your experimental manipulation. Therefore you need to use a statistical approach that tests the group average. We don’t want only people who are well trained at walking down corridors.
In contrast, in threshold psychophysics you don’t care about the “average person” but rather you want to know what the threshold performance is after all that other human noise – say inattention, hand-eye-coordination, fixation instability, uncorrected refractive error, mind-wandering, etc – has been excluded. Your research question is what is the just noticeable difference in stimuli under optimal conditions, not what is the just noticeable difference when distracted by thoughts about dinner or your inability to press the right button at the right time. A related (and more insidious) issue is also introspection. One could make the argument that many trained observers are also better judging the contents of their perceptual awareness than someone you recruited off the street (or your student participant pool). A trained observer may be quite adept at saying that the grating you showed appeared to them tilted slightly to the left – your Average Jo(sephine) may simply say that they noticed no difference. (This could in part be quantified by differences in response criterion but that is not guaranteed to work).
Taken together, the problem here is not with the small N approach – it is doubtless justified in many situations. Rather I wonder how to decide when it is justified. The cases described above seem fairly obvious but in many situations things can be more complicated. And to return to the main topic of this post, there could be insidious interactions between finding the right observers and your results. If I need trained observers for a particular experiment but I also want to find some who are naive to the purpose of the experiment, my inclusion criteria may bias the participants I end up with (this usually means your participants are all members of your department :P). For many purposes these biases may not matter. In some cases they probably do – for instance reports that visual illusions differ considerably in different populations. Ideally you want trained observers from all the groups you are comparing in this case.
If you’re on cog neuro twitter, you may have already come across an ongoing debate about a Verification Report by Chalkia et al. published in Cortex in 2020. A Verification Report is a new format at Cortex in which researchers can publish their attempts at reproducing the results of previously published research, in this case an influential study by Schiller et al, published 2010 in Nature. This caused a heated debate between them, the original authors, and also the handling editors at Cortex, which is still ongoing. While I am an editor at Cortex and work closely with the editors handling this particular case, I was not involved with that process. The particular research in question is outside my immediate expertise and there are a lot of gory details that I am ill-prepared to discuss. There is also room for yet another debate on how such scientific debates should be conducted – I don’t want to get into any of that here either.
However, this case reminded me of considerations I’ve had for quite some time. Much of the debate on this case revolves around the criteria by which data from participants were excluded in the original study. A student of mine has also been struggling in the past few months with the issue of data cleaning – specifically removing outlier data that clearly result from artifacts which would undeniably contaminate the results and lead us to draw undeniably false conclusions.
Data cleaning and artifact exclusion are important. You wouldn’t draw a star chart using a dirty telescope – otherwise that celestial object might just be a speck of dust on the lens. Good science involves checking that your tools work and removing data when things go wrong (and go wrong they inevitably will, even with the best efforts to maintain your equipment and ensure high data quality). In visual fMRI studies, some of the major measurement artifacts result from excessive head motion or poor fixation compliance. In psychophysical experiments, a lot depends on the reliability of participants at doing the tasks (some of which can be quite arduous), also about maintaining stable eye gaze, and even at introspecting about their perceptual experience. In EEG experiments, poor conductance in some electrodes may produce artifacts, and so on.
So it is obvious that sometimes data must be removed from a data set before we can make any inferences about our research question. The real question is what is the right way to go about doing that. An obvious answer is that these criteria must be defined a priori, before any data collection took place. In theory, this is where piloting is justified and could inform the range of parameters to be used in the actual experiments. A Registered Report would allow researchers to prespecify these criteria, vetted by independent reviewers. However, even long before anybody was talking about preregistration, researchers knew that data exclusion criteria should be defined upfront (it was literally one of the first things my PhD supervisor taught me).
Unfortunately, in truth this is not realistic. Your perfectly thought out criteria may simply be inappropriate in the face of real data. Your pilot experiment is likely “cleaner” than the final data set because you probably have a limited pool of participants to work with. No level of scrutiny by reviewers and editors of a Registered Report submission can foresee all eventualities and in fact sometimes fail miserably at predicting what will happen (I wonder in how far this speaks to the debates I’ve had in the past about the possibility of precognition :P).
An example from psychophysics
So what do you do then? In some cases the decision could be obvious. Using an example I used in a previous post (that I’m too lazy to dig up as it’s deep in the history of this blog), imagine I am running a psychophysics experiment. The resulting plots of participants should look something like this:
The x-axis is the stimulus level we presented to the participant, and the y-axis is their behavioural choice. But don’t worry about the details. The point is that the curve should have a sigmoidal shape. It might vary in terms of slope and where the 50% threshold (red dotted line) is but it generally should look similar to this plot. Now imagine one participant comes out like this:
This is obviously rubbish. Even if the choice of what is “obviously test/reference” are not really as obvious to the random participant as they are to the experimenter (and this happens often…), the curve should nonetheless have a general sigmoid shape and range from closer to 0% on the left to closer to 100% on the right. It most certainly should not start on the left at 50% and rise. I don’t know what happened in this particular case here (in fact I don’t even recall which experiment I took this from) but the most generous explanation is that the participant misunderstood the task instructions. Perhaps a more likely scenario is that they were simply bored and didn’t do the task at all and pressed response buttons at random. While this doesn’t explain why the curve is still rising to the right, that could perhaps be because they did the task to begin with – performing adequately on a few trials where “obviously test” was the correct response – but then gave up on it after a while.
Outlier removal and robust statistics
It doesn’t matter. Whatever the reason, this data set is clearly unusable. A simple visual inspection shows this but this is obviously subjective. This is a pretty clear example but where should we draw the line between a bad data set and a good one? Interestingly, a more objective, quantitative way to address this, the goodness of the sigmoidal curve fit, would be entirely inappropriate. The goodness-of-fit here may not be perfect but it’s clearly still a pretty close description of the data. No, our decision to reject this data set must be contingent on the outcome variables, the parameter fits of the sigmoid (the slope and threshold). But outcome contingent decisions are precisely one of those cardinal sins of analytic flexibility that we are supposed to avoid.
There are quantitative ways to clean such parameters posthoc by definiting a criterion for outliers. Often this will take the form of using the dispersion of the data (e.g., standard deviation, median absolute deviation, or some such measure) to reject values who fall a certain number of dispersion units from the group mean/median – for instance, people might remove all participants whose values fall +/-2 SDs from the mean. This can be reasonable in some situations because it effectively trims the distribution of your values. However, there is ample flexibility where you set this criterion and looking through the literature you will probably find anything from 1-3 SDs being used without any justification. Moreover, because your measure of dispersion is inherently related to how the data are distributed it is obviously affected by the outlier. A few very extreme and influential outliers can therefore mean that some obviously artifactual data are not flagged as outliers. To address this issue, several years ago we proposed to use bootstrapping to estimate the dispersion using a measure we called Shepherd’s Pi (the snark was strong with me then…).
In general, there are of course robust and/or non-parametric statistical tests that can help you make inferences on cases like this. While the details differ, what they have in common is that they are most robust in the face of certain kinds of outliers or in unsual data distributions. Some of them are so fierce that they will remove the majority of your observations – which is clearly absurd suggesting that the test may be ill-suited for this particular situation at least. There is a whole statistical literature on the development of these tests and comparing their performance. To anyone but a stats aficionado, this is very tedious and full of names and Greek letters (hence our snark…). What these kinds of robust statistics (and more arbitrary data cleaning methods like a dispersion criterion) are good for is robustness checks, a type of multiverse analysis where you compare the outcome of a range of tests to see if your results depend strongly on the particular test used. It seems sensible to include these checks, provided they are done transparently. There are obviously also situations where you might want to prespecify a particular test in a Registered Report, such as when you know that you expect a lot of outliers in a correlation you might preregister upfront that you will use Spearman’s correlation instead of the standard Pearson’s. You might even go so far as to adapt the use of a particular robust test a priori, even though it means you are sacrificing statistical power for improved robustness.
(Im-)practicalities and a way forward?
But the real issue is that this is clearly not asolution for the actual problem. In our example above, the blue data set is crap. Whatever your statistical criterions or robust statistical tests tell you, the blue data set should never enter our inference in the first place. Again, this is still a rather extreme example. It isn’t hard to justify posthoc why the curve shouldn’t start at 50% on the left – it violates the entire concept of the experiment. But most real situations are not so obvious. Sometimes we can make the argument that if participants perform at considerably less than ceiling/floor level for the “obvious” stimulus levels (left and right side of the plot in my example), that consistutes valid grounds for exclusion. We had this in a student project a few years ago where some participants performed at levels that – if they had done the task properly – really could only be because they were legally blind (which they obviously weren’t). It seems justified to exclude those participants, but it probably also underlines issues with the experiment: participants either had a tendency to misunderstand the task instructions, the task might have been to difficult for them, or the experimenter didn’t ensure that they did the experiment properly. If there are a lot of such participants, this flags up a problem that you probably want to fix in future experiments. In the worst case, it casts serious doubt on the whole experiment because if there are such problems for a lot of people how confident can we be that it isn’t affecting the “good” data sets, albeit in more subtle ways?
Perhaps the best way to deal with such problems is in the context of a Registered Report. This may seem counterintuitive. There have been numerous debates on how preregistration may stifle the necessary flexibility to deal with real data like this (I have been guilty of perpetuating these discussions myself for a time). This view still prevails in some corners. But actually the exact opposite is true. From my own (admittedly still limited) experience editing Registered Reports, I can say that it is not uncommon for authors to request alterations after they started data collection. In most cases, these are such minor changes that I wouldn’t bother the original reviewers with. They can simply be addressed by a footnote in the final submission. But of course in cases like our example here, where your dream of the preregistered experiment crashes against the rocky shores of real data, it may necessitate sending an alteration back to the reviewers who approved the preregistered design. There are valid scientific debates about which data should be included and excluded and there will inevitably be differences in opinion. That is completely fine. The point is that in this scenario you have a transparent record of the changes and why they were made, and you have independent experts weighing these arguments before the final outcome is known. Of course, a more practical solution could be to simply include the new outlier criterion as an additional, exploratory analysis in your final manuscript alongside the one you originally preregistered. However, in a situation like my example here this seems ill-advised: if the preregistered approach contains data that obviously shouldn’t be included, it isn’t worth very much. Some RR editors may take a stricter view on this, but I’d rather have an adapted design where the reason for changes are clearly justified and transparent and anyone can check the effects of these changes for themselves with the published data sets.
Transparency is really key. A Registered Report will provide some safety nets in terms of ensuring people declare the changes that were made and that they were reviewed by independent experts. But even in a classical (or exploratory) research article, the solution to this problem is simply transparent reporting. If data must be removed for justifiable posthoc reasons, then this should be declared explicitly. The excluded data should be made available so others can inspect it for themselves. Your mileage may vary with regard to some choices, but as long as it is clear why certain decisions were made this is simply a matter for debate. The big problem with all this is that the incentives in scientific publishing still work against this. As far as many high impact journals are concerned, data cleanliness is next to godliness. However justified the reasons may be, a study where some data were excluded posthoc inevitably looks messier than one where those exclusions are simply hidden.
Some have argued for rather Orwellian measures of publishing lab books with detailed records alongside research studies. I haven’t used a “lab book” since the mid-noughties. We have digital records of experiments we conducted, which are less prone to human error. Insofar as this is possible, such records are shared as part of published data sets. I have actually heard of some people who upload each experimental data set automatically as soon as it is collected. For one thing, this is only realistic for relatively small data (e.g. psychophysics or some cognitive psychology experiments perhaps). It doesn’t seem particularly feasible for a lot of research producing big files. It also just seems over-the-top to me. More importantly, this might be illegal in some jurisdictions (data sharing rules where I live are rather strict, in fact I sometimes wonder if any of my open science oriented colleagues aren’t breaking the law).
In the end, such ideas seem to treat the symptom and not the cause. We need to change the climate to make research more transparent. For this it is imperative that editors and reviewers remember that real data are messy. Obviously, if a result only emerges with extensive posthoc exclusions and the problems with the data set are mounting, there can be good reasons to question the finding. But it is crucial that researchers feel free to do the right thing.
This is a follow-up to my previous post. For context, you may wish to read this first. In that post I discussed how a plot from a Guardian piece (based on a policy paper) made the claim that German earners tend to misjudge themselves as being closer to the mean or, in the authors’ own words, “everyone thinks they’re middle class“. Now last week, I simply looked at this in the simplest way possible. What I think this plot shows is simply the effect of transforming a normal-ish data distribution into a quantile scale. For reference, here is the original figure again:
The column on the left aren’t data. They simply label the deciles, 10% brackets of the income distribution. My point previously was that if you calculate the means of the actual data for each decile you get exactly this line-squeeze plot that is shown here. Obviously this depends on the range of the scale you use. I simply transformed (normalised) the income data into a 1-10 scale where the maximum earner gets a score of 10 and everyone else is below. The point really is that in this scenario this has absolutely nothing to do with perceiving your income at all. It is simply plotting the normalised income data and you produce a plot that is highly reminiscent of the real thing.
Does the question matter?
Obviously my example wasn’t really mimicking what happens with perceived income. By design, it wasn’t supposed to. However, this seems to have led to some confusion about what my “simulation” (if you can even call it that) was showing. A blog post by Dino Carpentras argues that what matters here is how perceived income was measured. Here I want to show why I believe this isn’t the case.
First of all, Dino suggested that if people indeed reported their decile then the plot should have perfectly horizontal lines. Dino’s post already includes some very nice illustrations of that so I won’t rehash that here and instead encourage you to read that post. A similar point was made to me on Twitter by Rob McCutcheon. Now, obviously if people actually reported their true deciles then this would indeed be the case. In this case we are simply plotting the decile against the decile – no surprises there. In fact, almost the same would happen if they estimated the exact quantile they fall in and we then average that (that’s what I think Rob’s tweet is showing but I admit my R is too rusty to get into this right now).
My previous post implicitly assumed that people are not actually doing that. When you ask people to rate themselves on a 1-10 scale in terms of where their income lies, I doubt people will think about deciles. But keep in mind that the actual survey asked the participants to rate exactly that. Yet even in this case, I doubt that people are naturally inclined to think about themselves in terms of quantiles. Humans are terrible at judging distributions and probability and this is no exception. However, this is an empirical question – there may well be a lot of research on this already that I’m unaware of and I’d be curious to know about it.
But I maintain that my previous point still stands. To illustrate, I first show what the data would look like in these different scenarios if people could indeed judge their income perfectly on either scale. The plot below is showing what I used in my example previously. This is a distribution of (simulated) actual incomes. The x-axis shows the income in fictitious dollars. All my previous simulation did was to normalise so the numbers/ticks on the x-axis are changed to be between 1-10 but all the relationships remain the same.
But now let us assume that people can judge their income quantile. This comes with a big assumption that all survey respondents even know what that means, which I’d doubt strongly. But let’s take that granted that any individual is able to report accurately what percentage of the population earns less than them. Below I plot that on the y-axis against the actual income on the x-axis. It gives you the characteristic sigmoid shape – it’s a function most psychophysicists will be very familiar with: the cumulative Gaussian.
If we averaged the y-values for each x-decile and plotted this the way the original graph did, we would get close to horizontal lines. That’s the example I believe Rob showed in his tweet above. However, Dino’s post goes further and assumes people can actually report their deciles (that is, answer the question the survey asked perfectly). That is effectively rounding the quantile reports into 10% brackets. Here is the plot of that. It still follows the vague sigmoid shape but becomes sharply edged.
If you now plotted the line squeeze diagram used in the original graph, you would get perfectly horizontal lines. As I said, I won’t replot this; there really is no need for it. But obviously this is not a realistic scenario. We are talking about self-ratings here. In my last post I already elaborated on a few psychological factors why self-rating measures will be noisy. This is by no means exhaustive. There will be error on any measure, starting from simple mistakes in self-report or whatever. While we should always seek to reduce the noise in our measurements, noisy measurements are at the heart of science.
So let’s simulate that. Sources of error will affect the “perceived income” construct at several levels. The simplest we can do to simulate it is an error on how much the individual thinks their actual income is – we take each person’s income and add a Gaussian error. I used a Gaussian with SD=$30,000. That may be excessive but we don’t really know that. There is likely error in how high people think their income is relative to their peers and general spending power. Even more likely, there must be error on how they rate themselves on the 1-10 decile scale. I suspect that when transformed back into actual income this will be disproportionally larger than the error on judging their own income in dollars. It doesn’t really matter in principle.
Each point here is a simulated person’s self-reported income quantile plotted against their actual income. As you can see while the data still follow the vague sigmoid shape, there is a lot of scatter in people’s “reported” quantiles compared to what it actually should be. For clarity, I added a colour code here which denotes the actual income decile each person belongs to. The darkest blue are the 10% lowest earners and the yellow bracket is the top earners.
Next I round people’s income to simulate their self-reported deciles. The point of this is to effectively transform the self-reports into the discrete 1-10 scale that we believe the actual survey respondents used (I still don’t know the methods and if people were allowed to score themselves a 5.5 for instance – but based on my reading of the paper the scale was discrete). I replot these self-reported deciles using the same format:
Obviously, the y-axis will now again cluster in these 10 discrete levels. But as you can see from the colour code, the “self-reported” decile is a poor reflection of the actual income bracket. While a relative majority (or plurality) of respondents scoring themselves 1 are indeed in the lowest decile, in this particular example some of them are actual top earners. The same applies to the other brackets. Respondents thinking of themselves as perfectly middle class in decile 5 actually come more or less equally from across the spectrum. Now, again this may be a bit excessive but bear with me for just a while longer…
What happens when we replot this with our now infamous line plots? Voilà, doesn’t this look hauntingly familiar?
The reason for this is that perceived income is a psychological measure. Or even just a real world measure. It is noisy. The take-home message here is: It does not matter what question you ask the participants. People aren’t computers. The corollary of that is that when data are noisy the line plot must necessarily produce this squeezing effect the original study reported.
Now you may rightly say, Sam, this noise simulation is excessive. That may well be. I’ll be the first to admit that there are probably not many billionaires who will rate themselves as belonging to the lowest decile. However, I suspect that people indeed have quite a few delusions about their actual income. This may be more likely to affect the people in the actual middle range perhaps. So I don’t think the example here is as extreme as it may appear at first glance. There are also many further complications, such as that these measures are probably heteroscedastic. The error by which individuals misjudge their actual income level in dollars is almost certainly greater for high earners. My example here is very simplistic in assuming the same amount of error across the whole population. This heteroscedasticity is likely to introduce further distortions – such as the stronger “underestimation” by top earners compared to the “overestimation” by low earners, i.e. what the original graph purports to show.
In any case, the amount of error you choose for the simulation doesn’t affect the qualitative pattern. If people are more accurate at judging their income decile, the amount of “squeezing” we see in these line plots will be less extreme. But it must be there. So any of these plots will necessarily contain a degree of this artifact and thus make it very difficult to ascertain if this misestimation claimed by the policy paper and the corresponding Guardian piece actually exists.
Finally, I want to reiterate this because it is important: What this shows is that people are bad at judging their income. There is error on this judgement, but crucially this is Gaussian (or semi-Gaussian) error. It is symmetric. Top earner Jeff may underestimate his own income because he has no real concept of how the other half** live. In contrast, billionaire Donny may overestimate his own wealth because of his fragile ego and he forgot how much money he wastes on fake tanning oil. The point is, every individual*** in our simulated population is equally likely to over- or under-estimate their income – however, even with such symmetric noise the final outcome of this binned line plot is that the bin averages trend towards the population mean.
*) Well, perhaps almost everything?
**) Or to be precise, how the other 99.999% live.
***) Actually because my simulation prevents negative incomes for the very lowest earners, the error must skew their perceived income upwards.
Matlab code for this simulation is available here.
I can hear you singing in the distance I can see you when I close my eyes Once you were somewhere and now you’re everywhere
Superblood Wolfmoon – Pearl Jam
If you read my previous blog post you’ll know I have a particular relationship these days with regression to the mean – and binning artifacts in general. Our recent retraction of a study reminded me of this issue. Of course, I was generally aware of the concept, as I am sure are most quantitative scientists. But often the underlying issues are somewhat obscure, which is why I certainly didn’t immediately clock on to them in our past work. It took a collaborate group effort with serendipitous suggestions, much thinking and simulating and digging, and not least of all the tireless efforts of my PhD student Susanne Stoll to uncover the full extent of this issue in our published research. We also still maintain that this rabbit hole goes a lot deeper because there are numerous other studies that used similar analyses. They must by necessity contain the same error – hopefully the magnitude of the problem is less severe in most other studies so that their conclusions aren’t all completely spurious. However, we simply cannot know that until somebody investigates this empirically. There are several candidates out there where I think the problem is almost certainly big enough to invalidate the conclusions. I am not the data police and I am not going to run around arguing people’s conclusions are invalid without A) having concrete evidence and B) having talked to the authors personally first.
What I can do, however, is explain how to spot likely candidates of this problem. And you really don’t have far too look. We believe that this issue is ubiquitous in almost all pRF studies; specifically, it affects all pRF studies that use any kind of binning. There are cases where this is probably of no consequence – but people must at least be aware of the issue before it leads to false assumptions and thus erroneous conclusions. We hope to publish another article in the future that lays out this issue in some depth.
But it goes well beyond that. This isn’t a specific problem with pRF studies. Many years before that I had discussions with David Shanks about this subject when he was writing an article (also long since published) of how this artifact confounds many studies in the field of unconscious processing, something that certainly overlaps with my own research. Only last year there was an article arguing that the same artifact explains the Dunning-Kruger effect. And I am starting to see this issue literally everywhere1 now… Just the other day I saw this figure on one of my social media feeds:
This data visualisation makes a striking claim with very clear political implications: High income earners (and presumably very rich people in general) underestimate their wealth relative to society as a whole, while low income earners overestimate theirs. A great number of narratives can be spun about this depending on your own political inclinations. It doesn’t take much imagination to conjure up the ways this could be used to further a political agenda, be it a fierce progressive tax policy or a rabid pulling-yourself-up-by-your-own-bootstraps type of conservatism. I have no interest in getting into this discussion here. What interests me here is whether the claim is actually supported by the evidence.
There are a number of open questions here. I don’t know how “perceived income” is measured exactly2. It could theoretically be possible that some adjustments were made here to control for artifacts. However, taken at face value this looks almost like a textbook example of regression to the mean. Effectively, you have an independent variable, the individuals’ actual income levels. We can presumably regard this as a ground truth – an individual’s income is what it is. We then take a dependent variable, perceived income. It is probably safe to assume that this will correlate with actual income. However, this is not a perfect correlation because perfect correlations are generally meaningless (say correlating body height in inches and centimeters). Obviously, perceived income is a psychological measure that must depend on a whole number of extraneous factors. For one thing, people’s social networks aren’t completely random but we all live embedded in a social context. You will doubtless judge your wealth relative to the people you mostly interact with. Another source of misestimation could be how this perception is measured. I don’t know how that was done here in detail but people were apparently asked to self-rate their assumed income decile. We can expect psychological factors at play that make people unlikely to put themselves in the lowest or highest scores on such a scale. There are many other factors at play but that’s not really important. The point is that we can safely assume that people are relatively bad at judging their true income relative to the whole of society.
But to hell with it, let’s just disregard all that. Instead, let us assume that people are actually perfectly accurate at judging their own income relative to society. Let’s simulate this scenario3. First we draw 10,000 people a Gaussian distribution of actual incomes. This distribution has a mean of $60,000 and a standard deviation of $20,000 – all in fictitious dollars which we assume our fictitious country uses. We assume these are based on people’s paychecks so there is no error4 on this independent variable at all. I use the absolute values to ensure that there is no negative income. The figure below shows the actual objective income for each (simulated) person on the x-axis. The y-axis is just random scatter for visualisation – it has no other significance. The colour code denotes the income bracket (decile) each person belongs to.
Next I simulate perceived income deciles for these fictitious people. To do this we need to do some rescaling to get everyone on the scale 1-10, with 10 being highest top earner. However – and this is important – as per our (certainly false) assumption above, perceived income is perfectly correlated with actual income. It is a simple transformation to rescale it. Now, what happens when you average the perceived income in each of these decile brackets like that graph above did? I do that below, using the same formatting as the original graph:
I will leave it to you, gentle reader, to determine how this compares to the original figure. Why is this happening? It’s simple really when you think about it: Take the highest income bracket. This ranges widely from high-but-reasonable to filthy-more-money-than-you-could-ever-spend-in-a-lifetime rich. This is not a symmetric distribution. The summary statistics of these binned data will be heavily skewed. Its mean/median will be biased downward for the top income brackets and upwards for the low income brackets. Only the income decile near the centre will be approximately symmetric and thus produce an unbiased estimate. Or to put it in simpler terms: the left column simply labels the deciles brackets. The only data here is in the right column and all this plot really shows is that the incomes have a Gaussian-like distribution. This has nothing to do with perceptions of income whatsoever.
In discussions I’ve had this all still confuses some people. So I added another illustration. In the graph below I plot a normal distribution. The coloured bands denote the approximated deciles. The white dots on the X-axis show the mean for each decile. The distance between these dots is obviously not equal. They all trend to be closer to the population mean (zero) than to the middle of their respective bands. This bias is present for all deciles except perhaps the most central ones. However, it is most extreme for the outermost deciles because these have the most asymmetric distributions. This is exactly what the income plots above are showing. It doesn’t matter whether we are looking at actual or perceived income. It doesn’t matter at all if there is error on those measures or not. All that matters is the distribution of the data.
Now, as I already said, I haven’t seen the detailed methodology of that original survey. If the analysis made any attempt to mathematically correct for this problem then I’ll stand corrected5. However, even in that case, the general statistical issue is extremely wide-spread and this serves as a perfect example of how binning can result in widely erroneous conclusions. It also illustrates the importance of this issue. The same problem relates to pRF tuning widths and stimulus preferences and whatnot – but that is frankly of limited importance. But things like these income statistics could have considerable social implications. What this shows to me is two-fold: First, please be careful when you do data analysis. Whenever possible, feed some simulated data to your analysis to see if it behaves as you think it should. Second, binning sucks. I see it effing everywhere now and I feel like I haven’t slept in months6…
A very similar thing happened when I first learned about heteroscedasticity. I kept seeing it in all plots then as well – and I still do…
Many thanks to Susanne Stoll for digging up the source for these data. I didn’t see much in terms of actual methods details here but I also didn’t really look too hard. Via Twitter I also discovered the corresponding Guardian piece which contains the original graph.
Matlab code for this example is available here. I still don’t really do R. Can’t teach an old dog new tricks or whatever…
There may be some error with a self-report measure of people’s actual income although this error is perhaps low – either way we do not need to assume any error here at all.
Somehow I doubt it but I’d be very happy to be wrong.
There could however be other reasons for that…
If this post confused you, there is now a follow-up post to confuse you even more… 🙂
or How innocent assumptions can lead to wrong conclusions
I promised you a (neuro)science post. Don’t let the title mislead you into thinking we’re talking about world affairs and societal ills again. While pigeonholing is directly related to polarised politics or social media, for once this is not what this post is about. Rather, it is about a common error in data analysis. While there have been numerous expositions about similar issues throughout the decades – as we’ve learned the hard way, it is a surprisingly easy mistake to make. A lay summary and some wider musings on the scientific process was published by Benjamin de Haas. A scientific article by Susanne Stoll laying out this problem in more detail is currently available as a preprint.
In science you often end up with large data sets, with hundreds or thousands of individual observations subject to considerable variance. For instance, in my own field of retinotopic population receptive field (pRF) mapping, a given visual brain area may have a few thousand recording sites, and each has a receptive field position. There are many other scenarios of course. It could be neural firing, or galvanic skin responses, or eye positions recorded at different time points. Or it could be hundreds or thousands of trials in a psychophysics experiment etc. I will talk about pRF mapping because this is where we recently encountered the problem and I am going to describe how it has affected our own findings – however, you may come across the same issue in many guises.
Imagine that we want to test how pRFs move around when you attend to a particular visual field location. I deliberately use this example because it is precisely what a bunch of published pRF studies did, including one of ours. There is some evidence that selective attention shifts the position of neuronal receptive fields, so it is not far-fetched that it might shift pRFs in fMRI experiments also. Our study for instance investigated whether pRFs shift when participants are engaged in a demanding (“high load”) task at fixation, compared to a baseline condition where they only need to detect a simple colour change of the fixation target (“low load”). Indeed, we found that across many visual areas pRFs shifted outwards (i.e. away from fixation). This suggested to us that the retinotopic map reorganises to reflect a kind of tunnel vision when participants are focussed on the central task.
What would be a good way to quantify such map reorganisation? One simple way might be to plot each pRF in the visual field with a vector showing how it is shifted under the attentional manipulation. In the graph below, each dot shows a pRF location under the attentional condition, and the line shows how it has moved away from baseline. Since there is a large number pRFs, many of which are affected by measurement noise or other errors, these plots can be cluttered and confusing:
Clearly, we need to do something to tidy up this mess. So we take the data from the baseline condition (in pRF studies, this would normally be attending to a simple colour change at fixation) and divide the visual field up into a number of smaller segments, each of which contains some pRFs. We then calculate the mean position of the pRFs from each segment under the attentional manipulation. Effectively, we summarise the shift from baseline for each segment:
This produces a much clearer plot that suggests some interesting, systematic changes in the visual field representation under attention. Surely, this is compelling evidence that pRFs are affected by this manipulation?
Unfortunately it is not1. The mistake here is to assume that there is no noise in the baseline measure that was used to divide up the data in the first place. If our baseline pRF map were a perfect measure of the visual field representation, then this would have been fine. However, like most data, pRF estimates are variable and subject to many sources of error. The misestimation is also unlikely to be perfectly symmetric – for example, there are several reasons why it is more likely that a pRF will be estimated closer to central vision than in the periphery. This means there could be complex and non-linear error patterns that are very difficult to predict.
The data I showed in these figures are in fact not from an attentional manipulation at all. Rather, they come from a replication experiment where we simply measured a person’s pRF maps twice over the course of several months. One thing we do know is that pRF measurements are quite robust, stable over time, and even similar between scanners with different magnetic field strengths. What this means is that any shifts we found are most likely due to noise. They are completely artifactual.
When you think about it, this error is really quite obvious: sorting observations into clear categories can only be valid if you can be confident in the continuous measure on which you base these categories. Pigeonholing can only work if you can be sure into which hole each pigeon belongs. This error is also hardly new. It has been described in numerous forms as regression to the mean and it rears its ugly head every few years in different fields. It is also related to circular inference, which has already caused a stir in cognitive and social neuroscience a few years ago. Perhaps the reason for this is that it is a damn easy mistake to make – but that doesn’t make the face-palming moment any less frustrating.
It is not difficult to correct this error. In the plot below, I used an independent map from yet another, third pRF mapping session to divide up the visual field. Then I calculated how the pRFs in each visual field segment shifted on average between the two experimental sessions. While some shift vectors remain, they are considerably smaller than in the earlier graph. Again, keep in mind that these are simple replication data and we would not really expect any systematic shifts. There certainly does not seem to be a very obvious pattern here – perhaps there is a bit of a clockwise shift in the right visual hemifield but that breaks down in the left. Either way, this analysis gives us an estimate of how much variability there may be in this measurement.
This approach of using a third, independent map loses some information because the vectors only tell you the direction and magnitude of the shifts, not exactly where the pRFs started from and where they end up. Often the magnitude and direction of the shift is all we really need to know. However, when the exact position is crucial we could use other approaches. We will explore this in greater depth in upcoming publications.
On the bright side, the example I picked here is probably extreme because I didn’t restrict these plots to a particular region of interest but used all supra-threshold voxels in the occipital cortex. A more restricted analysis would remove some of that noise – but the problem nevertheless remains. How much it skews the findings depends very much on how noisy the data are. Data tend to be less noisy in early visual cortex than in higher-level brain regions, which is where people usually find the most dramatic pRF shifts…
Correcting the literature
It is so easy to make this mistake that you can find it all over the pRF literature. Clearly, neither authors nor reviewers have given it much thought. It is definitely not confined to studies of visual attention, although this is how we stumbled across it. It could be a comparison between different analysis methods or stimulus protocols. It could be studies measuring the plasticity of retinotopic maps after visual field loss. Ironically, it could even be studies that investigate the potential artifacts when mapping such plasticity incorrectly. It is not restricted to the kinds of plots I showed here but should affect any form of binning, including the binning into eccentricity bins that is most common in the literature. We suspect the problem is also pervasive in many other fields or in studies using other techniques. Only a few years ago a similar issue was described by David Shanks in the context of studying unconscious processing. It is also related to warnings you may occasionally hear about using median splits – really just a simpler version of the same approach.
I cannot tell you if the findings from other studies that made this error are spurious. To know that we would need access to the data and reanalyse these studies. Many of them were published before data and code sharing was relatively common2. Moreover, you really need to have a validation dataset, like the replication data in my example figures here. The diversity of analysis pipelines and experimental designs makes this very complex – no two of these studies are alike. The error distributions may also vary between different studies, so ideally we need replication datasets for each study.
In any case, as far as our attentional load study is concerned, after reanalysing these data with unbiased methods, we found little evidence of the effects we published originally. While there is still a hint of pRF shifts, these are no longer statistically significant. As painful as this is, we therefore retracted that finding from the scientific record. There is a great stigma associated with retraction, because of the shady circumstances under which it often happens. But to err is human – and this is part of the scientific method. As I said many times before, science is self-correcting but that is not some magical process. Science doesn’t just happen, it requires actual scientists to do the work. While it can be painful to realise that your interpretation of your data was wrong, this does not diminish the value of this original work3 – if anything this work served an important purpose by revealing the problem to us.
We mostly stumbled across this problem by accident. Susanne Stoll and Elisa Infanti conducted a more complex pRF experiment on attention and found that the purported pRF shifts in all experimental conditions were suspiciously similar (you can see this in an early conference poster here). It took us many months of digging, running endless simulations, complex reanalyses, and sometimes heated arguments before we cracked that particular nut. The problem may seem really obvious now – it sure as hell wasn’t before all that.
This is why this erroneous practice appears to be widespread in this literature and may have skewed the findings of many other published studies. This does not mean that all these findings are false but it should serve as a warning. Ideally, other researchers will also revisit their own findings but whether or not they do so is frankly up to them. Reviewers will hopefully be more aware of the issue in future. People might question the validity of some of these findings in the absence of any reanalysis. But in the end, it doesn’t matter all that much which individual findings hold up and which don’t4.
Check your assumptions
I am personally more interested in taking this whole field forward. This issue is not confined to the scenario I described here. pRF analysis is often quite complex. So are many other studies in cognitive neuroscience and, of course, in many other fields as well. Flexibility in study designs and analysis approaches is not a bad thing – it is in fact essential for addressing scientific questions that we can adapt our experimental designs.
But what this story shows very clearly is the importance of checking our assumptions. This is all the more important when using the complex methods that are ubiquitous in our field. As cognitive neuroscience matures, it is critical that we adopt good practices in ensuring the validity of our methods. In the computational and software development sectors, it is to my knowledge commonplace to test algorithms on conditions where the ground truth is known, such as random and/or simulated data.
This idea is probably not even new to most people and it certainly isn’t to me. During my PhD there was a researcher in the lab who had concocted a pretty complicated analysis of single-cell electrophysiology recordings. It involved lots of summarising and recentering of neuronal tuning functions to produce the final outputs. Neither I nor our supervisor really followed every step of this procedure based only on our colleague’s description – it was just too complex. But eventually we suspected that something might be off and so we fed random numbers to the algorithm – lo and behold the results were a picture perfect reproduction of the purported “experimental” results. Since then, I have simulated the results of my analyses a few other times – for example, when I first started with pRF modelling or when I developed new techniques for measuring psychophysical quantities.
This latest episode taught me that we must do this much more systematically. For any new design, we should conduct control analyses to check how it behaves with data for which the ground truth is known. It can reveal statistical artifacts that might hide inside the algorithm but also help you determine the method’s sensitivity and thus allow you to conduct power calculations. Ideally, we would do that for every new experiment even if it uses a standard design. I realise that this may not always be feasible – but in that case there should be a justification why it is unnecessary.
Because what this really boils down to is simply good science. When you use a method without checking that it works as intended, you are effectively doing a study without a control condition – quite possibly the original sin of science.
In conclusion, I quickly want to thank several people: First of all, Susanne Stoll deserves major credit for tirelessly pursuing this issue in great detail over the past two years with countless reanalyses and simulations. Many of these won’t ever see the light of day but helped us wrap our heads around what is going on here. I want to thank Elisa Infanti for her input and in particular the suggestion of running the analysis on random data – without this we might never have realised how deep this rabbit hole goes. I also want to acknowledge the patience and understanding of our co-authors on the attentional load study, Geraint Rees and Elaine Anderson, for helping us deal with all the stages of grief associated with this. Lastly, I want to thank Benjamin de Haas, the first author of that study for honourably doing the right thing. A lesser man would have simply booked a press conference at Current Biology Total Landscaping instead to say it’s all fake news and announce a legal challenge5.
The sheer magnitude of some of these shifts may also be scientifically implausible, an issue I’ve repeatedly discussed on this blog already. Similar shifts have however been reported in the literature – another clue that perhaps something is awry in these studies…
Not that data sharing is enormously common even now.
It is also a solid data set with a fairly large number of participants. We’ve based our canonical hemodynamic response function on the data collected for this study – there is no reason to stop using this irrespective of whether the main claims are correct or not.
Although it sure would be nice to know, wouldn’t it?
Did you really think I’d make it through a blog post without making any comment like this?
A day may come when I will stop talking about conspiracy theories again, but it is not this day. There is probably nothing new about conspiracy theories – they have doubtless been with us since our evolutionary ancestors gained sentience – but I fear that they are a particularly troublesome scourge of our modern society. The global connectivity of the internet and social media enable the spread of this misinformation pandemic in unprecedented ways, just as our physical connectivity facilitate the spread of an actual virus. Also like an actual virus, they can be extremely dangerous and destructive.
But fear not, I will try to move this back to being a blog on neuroscience eventually :P. Today’s post is about some tools we can use to determine the plausibility of a hypothesis. I have written about this before. Science is all about formulating hypotheses and putting them to the test. Not all hypotheses are created equal however – some hypotheses are so obviously true they hardly need testing while others are so implausible that testing them is pointless. Using conspiracy theories as an example, here I will list some tools I use to spot what I consider to be highly implausible hypotheses. I think this is a perfect example, because despite the name conspiracy theories are not actually scientific theories at all – they are in fact conspiracy hypotheses and most are pretty damn implausible.
This is not meant to be an exhaustive list. There may be other things you can think of that help you determine that a claim is implausible, for example Carl Sagan’s chapter on The Fine Art of Baloney Detection. You can also relate much of this back to common logical fallacies. My post merely lists a few basic features that I frequently encounter out there in the wild. Perhaps you’ll find this list useful in your own daily face-palming experiences.
The Bond Villain
Is a central feature to this purported plot a powerful billionaire with infinite funding and unlimited resources and power at their disposal? Do they have a convoluted plan that just smells evil, such as killing off large parts of the world population for the “common good”? You know, like injecting them with vaccines that sterilise them?
The House of Cards
Is the convoluted plan so complicated and carefully crafted numerous steps in advance where each little event has to fall in place just right in order for it to work? You know, like using 5G tech to weaken people’s immune system so it starts a global pandemic with a virus you created in your secret lab so that everyone happily gets injected with your vaccine which will contain nanoscale microchips but not with any other vaccine that others might have developed in the meantime? And obviously you know your vaccine will work against the virus because you could test it thoroughly without anybody else finding out about it?
The Future Tech
Does the plan involve some technology you’ve first heard of on Star Trek or Doctor Who? Is a respiratory illness caused by mobile phone technology? Is someone injecting nanoscale computer chips with a vaccine? Is there brain scanning technology with spatial and temporal resolution that would render all of my research completely obsolete?
The Red Pill
Have you been living a lie all your life? Will embracing the idea mean that you have awoken and/or finally see what’s right in front of you? Are most other people brainwashed sheeple? Did a YouTube video by someone who’ve never heard of finally open your eyes to reality?
The Dull Razorblade
Is the idea built on multiple factors that are not actually necessary to explain the events that unfurled? Was a virus “obviously” created in a lab even though countless viruses occur naturally? Are the odds that what they claim happened more likely than that the same thing happened by chance? Is the most obvious explanation for why the motif of Orion’s Belt appears throughout history and the world because aliens visited from Rigel 7 and not because it’s one of the most recognisable constellations in the night sky?
The World Government
Does it require the deep cooperation of most governments in the world whilst they squabble and vehemently disagree in the public limelight? Is the nefarious scheme perpetrated by the United Nations, which are famous for always agreeing, being efficient, and never having any conflict? (Note that occasionally it may only be the European Union rather than the UN).
The Flawed Explanation
Are the individual hypotheses that form the bigger conspiracy mutually exclusive? Is it based on current geography or environmental conditions even though it happened hundreds, thousands, or millions of years in the past? Does it involve connecting dots on the Mercator world map in straight lines which would actually not be straight on the globe or any other map projection?
The Unlikely Saint
Is the person most criticised, ridiculed, or reviled by the mainstream media in fact the good guy? Imagine, if you will, a world leader who is a former intelligence operative and spy master and who has invaded several sovereign countries. Is he falsely accused of assassinating his enemies and pursuing a cold political plan and actually just a friendly, misunderstood teddy bear? Or perhaps that demagogue, who riles the masses with hateful rhetoric and who has committed acts of corruption in broad daylight, is in fact defending us from evil puppy eating monsters? The CEO of a fossil fuel company in truth protects us from all those environmentalist hippies in centre-right governments who want to poison us with clean air and their utopian idealism of a habitable planet?
The Vast Network
Is everyone in on it? All scientists including all authors, editors and peer reviewers and all the technical support staff and administrators, all influential political leaders and their aides, all medical doctors and nurses and pharmacists, all engineers and all school teachers are involved in this complex scheme to fool the unwashed masses even though there has never been a credible whistleblower? Have they remained silent even though the Moon Landing was hoaxed half a century ago? Do all scientists working on a vaccine for widespread disease actually want to inject you with nanoscale microchips? Is there fortunately a YouTuber whose videos finally lay bare this outrageous, evil scheme?
The Competent Masterminds
Does it assume an immense level of competence and skill on the part of political leaders and organisations to execute their nefarious convoluted plans in the face of clear evidence to the contrary? Are they all just acting like disorganised buffoons to fool us?
The Insincere Questions
Is the framer of the idea “merely asking questions”? Do they simply want you to “think for yourself”? Does thinking for yourself in fact mean agreeing with that person? Do they ask questions about who funded some scientific research without any understanding of how scientific research is actually funded? Are they “not saying it was aliens” but it is obvious that is was in fact aliens?
The Unfalsifiable Claims
Is there no empirical evidence that could prove the claim wrong? Is this argument going in circles or are the goalposts shifted? Is a fact-checking website untrustworthy because it is “obviously part of the conspiracy”, even though you can directly check their source material which is of course also all fabricated? Is the idea based on some claim that has been shown to be a fraud, and the fraudster has been discredited even by his co-authors, but naturally this just part of an even bigger cover-up and a smear campaign? Can only the purveyor of this conspiracy theory be trusted?
The Torrent of Praise
Is the comment section under this YouTube video or Facebook post a long list of people praising and commending the poster for their truth-telling and use of “evidence”? Do most of these commenters have numbers in their name? Do they have profile pictures that look strangely akin to stock photos? Do any of the comments concur with the original post by adding some anecdote that sounds like an episode of the X-Files?
The Puppet Masters
Does it mention the Elders or Zion, the Illuminati, the Knights Templar, or some similar sounding, secret organisation? Or perhaps the Deep State?
I would like to lodge a complaint. Ever since I was admitted to the cabal over a decade ago I have been waiting for my paycheck – but thus far the immense riches I was promised by the Science Illuminati have yet to materialise. If I had known sooner how much money a CEO in a multinational fossil fuel corporation makes, I’d have pursued that truthtelling career instead of pretending that air pollution is bad for your health and blowing unprecedented amounts of carbon dioxide into the atmosphere could have any consequences on the global climate.
I am also still waiting for the keys to the Ivory Tower. The Lords of Big Vaccine explicitly told us at the induction that these would be forthcoming within days of pledging allegiance to “conventional medicine”. Nobody ever died of the measles, smallpox, or polio. When do I finally get to use the mind-control chips in vaccines? Also, when do I get the antidote to the vaccines I was given before I was anointed as a scientific acolyte?
Now that the roll-out of 5G is well underway, I also hope that you will soon put this to some good use instead of simply causing pandemics with it. Rather we should use it to erase the memories of all those witless fools out there before the secret gets out. I have overheard people suggest they should “follow the money” when looking at scientific research. We really don’t want them to find out how deeply involved funding agencies are in how scientists decide what research they do, and how they have been falling all over themselves just to give us money.
Most importantly, I don’t know why I continue to publish articles in peer-reviewed journals. Why do I keep having these mind-numbing battles with Nitpicker #2? As we all know, this isn’t real “research”. The truths about the universe are best discovered through quick Google searches, our elderly relatives’ Facebook posts, and watching random dudes on YouTube. I understand that we need to keep up the illusion of a body of scientific knowledge and therefore we should publish lots of papers. But surely in that case we should make it easier to do so rather than throwing all those obstacles in our paths, like quibbling about statistics or discussing confounds. Is this why you created all those journals that keep emailing me to publish my eminent work in their inaugural issue?
I’ll be awaiting your reply urgently. If I don’t see all those millions of dollars soon, I might start to think that this conspiracy isn’t working out for me, and I might need to go public with what I know. Don’t think you can silence me by forcing me to wear a face mask!
It has been almost a year since I last posted on this blog. I apologise for this hiatus. I’m afraid it’ll continue as it will probably be even longer before my next post. I simply don’t have the time for the blog these days. But in a brief lull in activities I decided to write this well-overdue post. No, this is not yet another neuroscientist wheeling out his Dunning-Krugerism to make a simplistic and probably dead-wrong (no pun intended) model of the CoViD-19 pandemic, and I certainly won’t be talking about what the governments are doing right or wrong in handling this dreadful situation. But the post is at least moderately related to the pandemic and to this very issue of expertise, and more broadly to current world events.
Years ago, I was locked in an extended debate with parapsychology researchers about the evidence for so-called “psi” effects (precognition, telepathy, and the like). What made matters worse, I made the crucial mistake of also engaging in discussion with some of the social media followers of these researchers. I have since gotten a little wiser and learned about the futility and sanity-destroying nature of social media (but not before going through the pain of experiencing the horrors of social media in other contexts, not least of all Brexitrump). I now try my best (but sometimes still fail) to stay away from this shit and all the outrage junkies and drama royalty. Perhaps I just got tired…
Anyway, in the course of this discussion about “psi” research, I uttered following phrase (or at least this is it paraphrased – I’m too lazy to look it up):
To be a scientist, is to be a skeptic.
This statement was based on the notions of scientific scrutiny, objectively weighing evidence for or against a proposition, giving the null hypothesis a chance, and never to take anybody’s word for granted. It was driven by an idealistic and quite possibly naive belief in the scientific method and the excitement about scientific thinking in some popular circles. But I was wrong.
Taken on their own, none of these things are wrong of course. It is true that scientists should challenge dogma and widely-held assumptions. We should be skeptical of scientific claims and the same level of scrutiny should be applied to evidence confirming our predictions as to those that seem to refute them. Arguments from authority are logically fallacious and we shouldn’t just take somebody at their word simply because of their expertise. As fallible human beings we scientists can fool ourselves into believing something that actually isn’t true, regardless of expertise, and perhaps at times expertise can even result in deeply entrenched viewpoints, so it pays to keep an open mind.
But there’s too much of a good thing. Too much skepticism will lead you astray. There is a saying, that has been (mis-)attributed to various people in various forms. I don’t know who first said it and I don’t much care either:
It pays to keep an open mind, but not so open that your brains fall out.
Taken at face value, this may seem out-of-place. Isn’t an open mind the exact opposite of being skeptical? Isn’t the purpose of this quote precisely to tell people not to believe just about any nonsense? Yes and no. If you spend any time reading and listening to conspiracy theories – and I strongly advise you not to – then you’ll find that the admonition to keep an open mind is actually a major hallmark of this misguided and dangerous ideology. I’ve seen memes making the rounds that most people are “sheeple” and only those who have awoken to the truth see the world as it really is, and lots of other such crap. Conspiracy theorists do really keep a very open mind indeed.
A belief in wild-eyed conspiracies goes hand-in-hand with the utmost skepticism of anything that smells even remotely like the status quo or our current knowledge. It involves being open to every explanation out there – except to the one thing that is most likely true. It is the Trust No One philosophy. When I was a teenager, I enjoyed the X-Files. One of the my favourite video games, Deus Ex, was strongly inspired by a whole range of conspiracy theories. It is great entertainment but some people seem to take this message a little too much to heart. If you look into the plot of Deus Ex, you’ll find some haunting parallels to actual world events, from terrorist attacks on New York City to the pandemic we are experiencing now. Ironically, one could even spin conspiracies about the game itself for that reason.
Conspiracy theories are very much in fashion right now, probably helped by the fact that there is currently a lunatic in the White House who is actively promoting them. It would be all fun and games, if it were only about UFOs, Ancient Aliens, Flat Earth, or the yeti. Or even about the idea that us dogmatic scientists want to suppress the “truth” that precognition is a thing*. But it isn’t just that.
From the origins of the novel coronavirus disease over vaccinations to climate change, we are constantly bombarded by conspiratorial thinking and its consequences. People apparently set fire to 5G radio masts because of this. Trust in authorities and experts has been eroded all over the globe. The internet seems to facilitate the spread of these ideas so they become far more influential than they would have been in past decades – sometimes to very damaging effects.
Can we even blame people? It does become increasingly harder to trust anything or anybody. I have seen first-hand how many news media are more interested in publishing articles to make a political point than in providing factual accuracy. This may not even be deliberate; journalists work to tight deadlines and they are a struggling industry trying to keep financially afloat. Revelations about the origins of the Iraq War and scandals of collusion and election meddling, some of which may well be true conspiracies while others may be liberal pipe dreams (and many may fall into a grey area in between), don’t help to restore public trust. And of course public trust in science isn’t helped by the Replication Crisis**.
Science isn’t just about being skeptical
Sure, science is about challenging assumptions but it is also about weighing all available evidence. The challenging of assumptions we see in conspiracies is all too often cherry-picking. Science is also about the principle of parsimony and it requires us to determine the plausibility of claims. Crucially, it is also about acknowledging all the things we don’t know. That last point includes recognising that, you know, perhaps an expert in an area actually does occasionally know more about it than you.
No, you shouldn’t just believe anything someone says merely because they have PhD in the topic. And I honestly don’t know if expertise is really all that crucial in replicating social priming effects – this is for me where the issues with plausibility kick in. But knowing something about a topic gives experts insights that will elude an outsider and it would serve us well to listen to them. They should certainly have to justify and validate their claims – you shouldn’t just take their word as gospel. But don’t delude yourself into thinking you’ve uncovered “the Truth” by disbelieving everybody else. If I’ve learned anything from doing research, it is that the greatest delusion is when you think you’ve actually understood anything.
I have observed a worrying trend among some otherwise rather sensible people to brush aside criticism of conspiracy theories as smugness or over-confidence. This manifests in insinuations like these:
Of course, vaccines don’t cause autism, but perhaps this just distracts from the fact that they could be dangerous after all?
Of course, 5G doesn’t give people coronavirus but have governments used this pandemic as an opportunity to roll out 5G tech?
Of course, the CoViD-19 wasn’t manufactured in a Chinese lab, but researchers from the Wuhan Institute of Virologypublished studies on such coronaviruses and isn’t it possible that they already had the virus and it escaped the lab due to negligence or was even set loose on purpose?
Conspiracy theories are always dealing in possibilities. Of course, they require ardent believers to promote their tinfoil hat ideas. But they also feed on people like us, people with a somewhat skeptical and inquisitive mind who every so often fall prey to their own cognitive biases. Of course, all of these statements are possible – but that’s not the point. Science is not about what is possible but what is probable. Probabilities change as the evidence accumulates.
How plausible is the claim and even if it is plausible, is it more probable than other explanations or scenarios? Even if there were evidence that companies took advantage of the pandemic to roll out 5G (you know, this thing that has been debated for years and which had been planned ages before anyone even knew what a coronavirus is), wouldn’t it make sense to do this at a time when there is an unprecedented need of a world population in lockdown to have reliable and sophisticated mobile internet? Also, so fucking what? What concrete reason is it why you think 5G is a problem? Or are you just talking about the same itchy feeling people in past ages had about the internet, television, radio, and doubtless at some point also about books?
Let us for a moment ignore the blatant racism and various other factors that make this idea actually quite unlikely and accept the possibility that the coronavirus escaped from a lab in Wuhan. Why shouldn’t there be a lab studying animal-to-human transmission of viruses that have the potential for causing pandemics, especially since we already know this happened with numerous illnesses before and researchers have already warned years ago that such a coronavirus pandemic was coming? Doesn’t it make sense to study this at a place where this is likely to occur? What is more likely, that the thing that we know happens happened or that someone left a jar open by accident and let the virus escape the lab? How do you think the virus got in the lab in the first place? What makes it more likely that it escaped a lab than that it originated on a market where wild exotic animals are being consumed?
There is also an odd irony about some of these ideas. Anti-vaxxers seem somewhat quiet these days now that everybody is clamouring for a vaccine for CoViD-19. Perhaps that’s to be expected. But while there is literally no evidence that widely used vaccines are making you sick (at least beyond that weakened form of creating an immune response that makes you unsusceptible to the actually disease anyway) there are very good reasons to ask whether a new drug or treatment is safe. This is why researchers keep reminding us that a vaccine is still at least a year away and why I find recent suggestions one could become available even this September somewhat concerning. It is certainly great that so much work is put into fighting this pandemic and if human usage can begin soon that is obviously good news – but before we have wide global use perhaps we should ensure that this vaccine is actually safe. The plus side is, in contrast to anti-vaxxers, vaccine scientists are actually concerned about people’s health and well-being.
The real conspiracy
Ask yourself who stands to gain if you believe a claim, whether it is a scientific finding, an official government statement, or a conspiracy. Most conspiracy theories further somebody’s agenda. It could help somebody’s reelection or bring them political influence to erode trust in certain organisations or professions, but it could also be much simpler than that: clickbait makes serious money, and some people actually sow disinformation simply for the fun of it. We can be sure of one real conspiracy: the industry behind conspiracy theories.
* Still waiting for my paycheck for being in the pocket of Big Second-Law-of-Thermodynamics…
** This is no reason not to improve the replicability and transparency of scientific research – quite the opposite!