Friday 20 July 2018

Standing on the shoulders of giants, or slithering around on jellyfish: Why reviews need to be systematic

Yesterday I had the pleasure of hearing George Davey Smith (aka @mendel_random) talk. In the course of a wide-ranging lecture he recounted his experiences with conducting a systematic review. This caught my interest, as I’d recently considered the question of literature reviews when writing about fallibility in science. George’s talk confirmed my concerns that cherry-picking of evidence can be a massive problem for many fields of science.

Together with Mark Petticrew, George had reviewed the evidence on the impact of stress and social hierarchies on coronary artery disease in non-human primates. They found 14 studies on the topic, and revealed a striking mismatch between how the literature was cited and what it actually showed. Studies in this area are of interest to those attempting to explain the well-known socioeconomic gradient in health. It’s hard to unpack this in humans, because there are so many correlated characteristics that could potentially explain the association. The primate work has been cited to support psychosocial accounts of the link; i.e., the idea that socioeconomic influences on health operate primarily through psychological and social mechanisms. Demonstration of such an impact in primates is  particularly convincing, because stress and social status can be experimentally manipulated in a way that is not feasible in humans.

The conclusion from the review was stark: ‘Overall, non-human primate studies present only limited evidence for an association between social status and coronary artery disease. Despite this, there is selective citation of individual non-human primate studies in reviews and commentaries relating to human disease aetiology’(p. e27937).

The relatively bland account in the written paper belies the stress that George and his colleague went through in doing this work. Before I tried doing one myself, I thought that a systematic review was a fairly easy and humdrum exercise. It could be if the literature were not so unruly. In practice, however, you not only have to find and synthesise the relevant evidence, but also to read and re-read papers to work out what exactly was done. Often, it’s not just a case of computing an effect size: finding the numbers that match the reported result can be challenging. One paper in the review that was particularly highly-cited in the epidemiology literature turned out to have data that were problematic: the raw data shown in scattergraphs are hard to reconcile with the adjusted means reported in a summary (see Figure below). Correspondence sent to the author apparently did not achieve a reply, let alone an explanation.

Figure 2 from Shively and Thompson (1994) Arteriosclerosis and Thrombosis Vol 14, No 5. Yellow bar added to show mean plaque areas as reported in Figure 3 (adjusted for preexperimental thigh circumference and TPC-HDL cholesterol ratio)
Even if there were no concerns about the discrepant means, the small sample size and influential outliers in this study should temper any conclusions. But those using this evidence to draw conclusions about human health focused on the ‘five-fold increase’ in coronary disease in dominant animals who became subordinate.

So what impact has the systematic review achieved? Well, the first point to note is that the authors had a great deal of difficulty getting it accepted for publication: it would be sent to reviewers who worked on stress in monkeys, and they would recommend rejection. This went on for some years: the abstract was first published in 2003, but the full paper did not appear until 2012.

The second, disappointing conclusion comes from looking at citations of the original studies reviewed by Petticrew and Davey Smith in the human health literature since their review appeared. The systematic review garnered 4 citations in the period 2013-2015 and just one during 2016-2018. The mean citations for the 14 articles covered in their meta-analysis was 2.36 for 2013-2015, and 3.00 for 2016-2018. The article that was the source of the Figure above had six citations in the human health literature in 2013-2015 and four in 2016-2018. These numbers aren’t sufficient for more than impressionistic interpretation, and I only did a superficial trawl through abstracts of citing papers, so I am not in a position to determine if all of these articles accepted the study authors’ conclusions. However, the pattern of citations fits with past experience in other fields showing that when cherry-picked facts fit a nice story, they will continue to be cited, without regard to subsequent corrections,  criticism or even retraction.

The reason why this worries me is that the stark conclusion would appear to be that we can’t trust citations of the research literature unless they are based on well-conducted systematic reviews. Iain Chalmers has been saying this for years, and in his field of clinical trials these are more common than in other disciplines. But there are still many fields where it is seen as entirely appropriate to write an introduction to a paper that only cites supportive evidence and ignores a swathe of literature that shows null or opposite results. Most postgraduates have an initial thesis chapter that reviews the literature, but it's rare, at least in psychology, to see a systematic review - perhaps because this is so time-consuming and can be soul-destroying. But if we continue to cherry-pick evidence that suits us, then we are not so much standing on the shoulders of giants as slithering around on jellyfish, and science will not progress.

Thursday 12 July 2018

One big study or two small studies? Insights from simulations

At a recent conference, someone posed a question that had been intriguing me for a while: suppose you have limited resources, with the potential to test N participants. Would it be better to do two studies, each with N/2 participants, or one big study with all N?

I've been on the periphery of conversations about this topic, but never really delved into it, so I gave a rather lame answer. I remembered hearing that statisticians would recommend the one big study option, but my intuition was that I'd trust a result that replicated more than one which was a one-off, even if the latter was from a bigger sample. Well, I've done the simulations and it's clear that my intuition is badly flawed.

Here's what I did. I adapted a script that is described in my recent slides that give hands-on instructions for beginners on how to simulate data, The script, Simulation_2_vs_1_study_b.R, which can be found here, generates data for a simple two-group comparison using a t-test. In this version, on each run of the simulation, you get output for one study where all subjects are divided into two groups of size N, and for two smaller studies each with half the number of subjects. I ran it with various settings to vary both the sample size and the effect size (Cohen's d). I included the case where there is no real difference between groups (d = 0), so I could estimate the false positive rate as well as the power to detect a true effect.

I used a one-tailed t-test, as I had pre-specified that group B had the higher mean when d > 0. I used a traditional approach with p-value cutoffs for statistical significance (and yes, I can hear many readers tut-tutting, but this is useful for this demonstration….) to see how often I got a result that met each of three different criteria:
  • a) Single study, p < .05 
  • b) Split sample, p < .05 replicated in both studies 
  • c) Single study, p < .005

Figure 1 summarises the results.
Figure 1

The figure is pretty busy but worth taking a while to unpack. Power is just the proportion of runs of the simulation where the significance criterion was met. It's conventional to adopt a power cutoff of .8 when deciding on how big a sample to use in a study. Sample size is colour coded, and refers to the number of subjects per group for the single study. So for the split replication, each group has half this number of subjects. The continuous line shows the proportion of results where p < .05 for the single study, the dotted line has results from the split replication, and the dashed line has results from the single study with more stringent significance criterion, p < .005 .

It's clear that for all sample sizes and all effect sizes, the one single sample is much better powered than the split replication.

But I then realised what had been bugging me and why my intuition was different. Look at the bottom left of the figure, where the x-axis is zero: the continuous lines (i.e., big sample, p < .05) all cross the y-axis at .05. This is inevitable: by definition, if you set p < .05, there's a one in 20 chance that you'll get a significant result when there's really no group difference in the population, regardless of the sample size. In contrast, the dotted lines cross the y-axis close to zero, reflecting the fact that when the null hypothesis is true, the chance of two samples both giving p < .05 in a replication study is one in 400 (.05^2 = .0025). So I had been thinking more like a Bayesian: given a significant result, how likely was it to have been come from a population with a true effect rather than a null effect? This is a very different thing from what a simple p-value tells you*.

Initially, I thought I was onto something. If we just stick with p < .05, then it could be argued that from a Bayesian perspective, the split replication approach is preferable. Although you are less likely to see a significant effect with this approach, when you do, you can be far more confident it is a real effect. In formal terms, the likelihood ratio for a true vs null hypothesis, given p < .05, will be much higher for the replication.

My joy at having my insight confirmed was, however, short-lived. I realised that this benefit of the replication approach could be exceeded with the single big sample simply by reducing the p-value so that the odds of a false positive are minimal. That's why Figure 1 also shows the scenario for one big sample with p < .005: a threshold that has recently proposed as a general recommendation for claims of new discoveries (Benjamin et al, 2018)**.

None of this will surprise expert statisticians: Figure 1 just reflects basic facts about statistical power that were popularised by Jacob Cohen in 1977. But I'm glad to have my intuitions now more aligned with reality, and I'd encourage others to try simulation as a great way to get more insights into statistical methods.

Here is the conclusions I've drawn from the simulation:
  • First, even when the two groups come from populations with different means, it's unlikely that you'll get a clear result from a single small study unless the effect size is at least moderate; and the odds of finding a replicated significant effect are substantially lower than this.  None of the dotted lines achieves 80% power for a replication if effect size is less than .3 - and many effects in psychology are no bigger than that. 
  • Second, from a statistical perspective, testing an a priori hypothesis in a larger sample with a lower p-value is more efficient than subdividing the sample and replicating the study using a less stringent p-value.
I'm not a stats expert, and I'm aware that there's been considerable debate out there about p-values - especially regarding the recommendations of Benjamin et al (2018). I have previously sat on the fence as I've not felt confident about the pros and cons. But on the basis of this simulation, I'm warming to the idea of p < .005. I'd welcome comments and corrections.

*In his paper The reproducibility of research and the misinterpretation of p-values. Royal Society Open Science, 4(171085). doi:10.1098/rsos.171085 David Colquhoun (2017) discusses these issues and notes that we also need to consider the prior likelihood of the null hypothesis being true: something that is unknowable and can only be estimated on the basis of past experience and intuition.
**The proposal for adopting p < .005 as a more stringent statistical threshold for new discoveries can be found here: Benjamin, D. J., Berger, J. O., Johannesson, M., Nosek, B. A., Wagenmakers, E. J., Berk, R., . . . Johnson, V. E. (2018). Redefine statistical significance. Nature Human Behaviour, 2(1), 6-10. doi:10.1038/s41562-017-0189-z

Postscript, 15th July 2018

This blogpost has generated a lot of discussion, mostly on Twitter. One point that particularly interested me was a comment that I hadn’t done a fair comparison between the one-study and two-study situation, because the plot showed a one-off two group study with an alpha at .005, versus a replication study (half sample size in each group) with alpha at .05. For a fair comparison, it was argued, I should equate the probabilities between the two situations, i.e. the alpha for the one-off study should be .05 squared = .0025.

So I took a look at the fair comparison: Figure 2 shows the situation when comparing one study with alpha set to .0025 vs a split replication with alpha of .05. The intuition of many people on Twitter was that these should be identical, but they aren’t. Why not? We have the same information in the two samples. (In fact, I modified the script so that this was literally true and the same sample was tested singly and again split into two – previously I’d just resampled to get the smaller samples. This makes no difference – the single sample with more extreme alpha still gives higher power).

Figure 2: Power for one-off study with alpha .0025 (dashed lines) vs. split replication with p < .05
To look at it another way, in one version of the simulation there were 1600 simulated experiments with a true effect (including all the simulated sample sizes and effect sizes). Of these 581 were identified as ‘significant’ both by the one-off study with p < .0025 and they were also replicated in two small studies with p < .05. Only 5 were identified by the split replication alone, but 134 were identified by the one-off study alone.

I think I worked out why this is the case, though I’d appreciate having a proper statistical opinion. It seems to have to do with accuracy of estimating the standard deviation. If you have a split sample and you estimate the mean from each half (A and B), then the average of mean A and mean B will be the same as for the big sample of AB combined. But when it comes to estimating the standard deviation – which is a key statistic when computing group differences – the estimate is more accurate and precise with the large sample. This is because the standard deviation is computed by measuring the difference of each value from its own sample mean. Means for A and B will fluctuate due to sampling error, and this will make the estimated SDs less reliable. You can estimate the pooled standard deviation for two samples by taking the square root of the average of the variances. However, that value is less precise than the SD from the single large sample. I haven’t done a large number of runs, but a quick check suggests that whereas both the one-off study and the split replication give pooled estimates of the SD at around the true value of 1.0, the standard deviation of the standard deviation (we are getting very meta here!) is around .01 for the one-off study but .14 for the split replication. Again, I’m reporting results from across all the simulated trials, including the full range of sample sizes and effect sizes.

Figure 3: Distribution of estimates of pooled SD; The range is narrower for the one-off study (pink) than for the split replication studies (blue). Purple shows area of overlap of distributions

This has been an intriguing puzzle to investigate, but in the original post, I hadn’t really been intending to do this kind of comparison - my interest was rather in making the more elementary point which is that there's a very low probability of achieving a replication when sample size and effect size are both relatively small.

Returning to that issue, another commentator said that they’d have far more confidence in five small studies all showing the same effect than in one giant study. This is exactly the view I would have taken before I looked into this with simulations; but I now realise this idea has a serious flaw, which is that you’re very unlikely to get those five replications, even if you are reasonably well powered, because – the tldr; message implicit in this post – when we’re talking about replications, we have to multiply the probabilities, and they rapidly get very low. So, if you look at the figure, suppose you have a moderate effect size, around .5, then you need a sample of 48 per group to get 80% power. But if you repeat the study five times, then the chance of getting a positive result in all five cases is .8^5, which is .33. So most of the time you’d get a mixture of null and positive results. Even if you doubled the sample size to increase power to around .95, the chance of all five studies coming out positive is still only .95^5 (82%).

Finally, another suggestion from Twitter is that a meta-analysis of several studies should give the same result as a single big sample. I’m afraid I have no expertise in meta-analysis, so I don’t know how well it handles the issue of more variable SD estimates in small samples, but I’d be interested to hear more from any readers who are up to speed with this.