2/n Study is here: https://www.medrxiv.org/content/10.1101/2020.05.13.20101253v3 …
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3/n You can find my original thread on the paper here:https://twitter.com/GidMK/status/1262956011872280577?s=20 …
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4/n So, what's changed? At first glance, not much. The median IFR has gone up from 0.26% to 0.27%, based on the inclusion of a bunch more studiespic.twitter.com/b8tpzY2Y53
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5/n Some of the more inappropriate statements have at last been removed, such as the age-related stuff and the incorrect citation of the case-fatality rate of influenza Good!
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6/n On the downside, we now have this comparison with the death rates from flu, which is also just...weird If nothing else, the COVID-19 pandemic is STILL GROWING and has ALREADY killed as many people as a 'bad' influenza seasonpic.twitter.com/Et7Ofqt8LI
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7/n Also, many of the issues I've raised previously are still there. Many studies have been included that probably aren't reliable estimates of population seroprevalence are lumped in with very good estimates That's...less than ideal
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8/n Let me illustrate with an example This study has been included to calculate IFRs for 4 regions of China - Hubei (not Wuhan), Chonqing, Sichuan, and Guangdongpic.twitter.com/fZFInUGuHU
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9/n So the author has taken the percent positive of antibody tests for COVID-19 from each of the regions represented in the study, and used that as a population estimate for the entire region to calculate IFR But is this reasonable?
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10/n The study only tested two groups: healthcare workers and people on dialysis Now, Ioannidis excludes any testing on healthcare workers, but dialysis patients are...fine?pic.twitter.com/4tYTh4dwNT
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11/n And these high numbers of seropositive estimates led to inferred IFRs for these four places in China of 0.00%!pic.twitter.com/zkMNza7NNo
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12/n If nothing else, the numbers here imply that 99.9996% of all infections in Chongqing were asymptomatic (500 official cases, widespread testing, but seropositivity of 3.8% in the study implying 12 million 'true' cases) Is this plausible???pic.twitter.com/qSm99jQ0Kw
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13/n There are also some numbers in this revised paper that are wrong This figure should read 44%, not 47%pic.twitter.com/xccqCxh6Om
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14/n Moreover, in the example highlighted above, the IFR calculated is for Brooklyn, but this was only true for a tiny subset of 240 patients in this 28,523 patient study. The IFR calculation should've been for the whole of NYC, not just Brooklyn!pic.twitter.com/178IRcCQ3x
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15/n There are also some worrying inconsistencies in how Ioannidis has split up studies that sampled multiple places within countries
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16/n For example, the ENE-COVID and Brazilian studies, which sampled entire countries by region, are only summed up as a single valuepic.twitter.com/6295tiG91O
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17/n On the other hand, several studies that sampled multiple regions (but found MUCH lower IFRs) in other places are split up by area I cannot see any explanation for this in the paperpic.twitter.com/sdMyr7qGCo
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18/n On top of this, we've got another problem - collinearity The basic issue is that you shouldn't lump multiple samples of the same group of people together into one study
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19/n But now, in the study we have Wuhan (A), Wuhan (B), and Hubei (not Wuhan) It's very poor statistical practice to lump all these estimates together like this
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20/n Similarly, we have two estimates from Spain. One is the ENE-COVID study, a rigorous randomized seroprevalence study that is the envy of the world The other is a non-random sample of pregnant women at one place in Barcelona These are given EQUAL WEIGHTS in the analysispic.twitter.com/j2r5CLKGlj
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21/n The Spain example is even more of a problem because the ENE-COVID (the rigorous study) implies an IFR in Barcelona of ~1% The survey of pregnant women implies ~.5% Guess which one is used?pic.twitter.com/1JO5aNfrbV
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22/n Now, all of this collinearity is particularly troubling for that 0.27% estimate that I mentioned way back at the start of the thread
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23/n If we get average the collinear results - where we've included the same study or the same sample multiple times - the median jumps immediately to 0.35% That's quite a bit higher!
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24/n But there are more corrections to be made. In several places, the IFR that is in this paper does not match the IFR calculated by the study authors
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25/n For example, Geneva. The original authors calculated an IFR of 0.64%, but this is downgraded to 0.45% in the paperpic.twitter.com/lEEG7LPjez
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26/n And this is not the only example. Another study tested over three weeks and found seroprevalence of 3.85%, then 8.36%, then 1.46%. Overall 3.53% The 8.36% figure is used, giving 5x more infections than the study itself found, and the lowest IFR possiblepic.twitter.com/ZeC8arsL7P
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27/n Taking all this into account, let's look at the IFRs for only those studies using representative population samples that were correctly calculated
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28/n Here's the revised table. The lowest IFR is, again, Ioannidis' own study, at 0.18%. Nearly half of the estimates are above 1%, and they range all the way up to 1.63% (!)pic.twitter.com/7xU7DGrq2Q
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29/n Somehow, for the third time running, there are innumerable decisions made in the paper that seem to only ever push down the IFR, rather than produce the best estimate
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30/n As I've outlined, there are also a number of simple errors that make this very problematic as an estimate of the IFR (or the IFR range) for COVID-19
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31/n All that being said, the discussion is now MUCH better, and really engages with some of the things I (and others) discussed in previous threads. Too much to go over here, but well worth a read
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