Big Data, Plainly Spoken (aka Numbers Rule Your World)

Too good to be true instinct

Good data analysts have developed an instinct of perking up when results are "too good to be true". This is a must-have attribute that I'm always looking for in a job candidate. It is a protective instinct, a response that protects the analysts from getting fooled by the data. Nassim Taleb called this type of thing "fooled by randomness". The temptation is not randomness itself but the lack thereof.

(Credit: Sonja Alves, Flickr)

Observational studies of the Covid-19 vaccines are a case in point. I have been spooked by the consistency of estimates of vaccine effectiveness. Almost all peer-reviewed studies and most working papers that get mainstream attention contain values of VE that are in the 70-90 percent range. (Since these are relative ratios, a 50-percent multiple improvement is already a huge effect.) There is a consistency across headline results of different studies, and there is also a consistency of values inside individual studies, across segments, using different outcome metrics, different methodologies, etc. etc.

Below is Table 2 from the traffic accidents study that I have been reviewing (link):

The aggregate result (derived from the inadmissible non-adjusted comparison discussed in the first post of this series) is shown in the last row and represents a value of 1.7x. The rows above come from applying the same methodology to subsets of the study population, some of them are mutually exclusive while others are overlapping. Most of the values line up close to or near that 1.7x value. There is only one segment (over 65) that has the opposite direction but barely. What does this consistency tell us?

Shown below is the top part of Table 3. Here, the researchers analyzed many variants of the outcome, applying the same analytical strategy. Whereas Figure 2 above shows any involvement in traffic accidents, Table 3 below breaks down these accidents into subtypes, like involvement as driver versus pedestrian, time of day and so on.

The consistency is once again remarkable. Whereas the aggregate number is shown as 1.7x (top row), all the other numbers ranged from 1.5x to 5.1x. Almost all the variance is on the high side of the aggregate. What does such consistency tell us?

In the Appendix, the authors rolled out even more rows of analysis:

Again, all effects are in the range 1.4x to 1.7x. What does this consistency mean? That's what I want to explore in this post.

***

In the mainstream, such consistency is portrayed as resounding evidence. Each individual study that generates another impressive relative ratio similar to the previous result is regarded as another confirmation. The authors of the traffic accidents study believe that because everywhere they looked, they saw the same consistent number, it must mean that they have found something really important - like Newton's Law of Gravity.

Unlike Newton, they aren't studying the realm of physics. The study's data concern human behavior, and social behavior, and it is actually shocking, rather than comforting, to find a law of nature in this arena. My prior - from decades looking at data about humans - is that (a) aggregate effects are typically small, so that even a 10% improvement is remarkable, and (b) there is substantial variability when looking across different segments, different metrics, etc., which is another way to say that "interaction effects" are important.

Were these researchers, mainstream scientists, and the mass media being fooled by (lack of) randomness?

***

Other than discovering some immutable law of nature, what are other possible explanations for the remarkable consistency?

File Drawer Effect

Let's say there is a medical journal editor who only publishes vaccine studies that show high vaccine efficacy - since anything else has little societal value. The result of this editorial practice is that (almost) every study that sees the light of day will definitely have a VE estimate above some lower bound (say, 70%). In this scenario, the consistency of all the peer-reviewed results may have nothing to do with the vaccines themselves, but can be explained by publication bias that is filtering out studies below that bound. This bias is sometimes called the "file drawer effect," describing researchers who stack away "failed" studies (e.g. p-value > 5%) in their file cabinets since journals would reject them.

A consequence of the file drawer effect is that the average of the published results over-estimates the true vaccine efficacy.

In the context of Covid-19 vaccines, the file drawer effect may be related to the phenomonon of cargo cult science.

 

Cargo Cult Science

Cargo cult science is a term coined by physicist Richard Feynman. Roughly speaking, he warns against the potential of bad science even when scientists follow so-called best practices.

Other than the initial clinical trials conducted in 2020 (which were scientifically aborted upon emergency use authorization when the placebo groups were destroyed), all evidence of Covid-19 vaccine efficacy have come from observational datasets. All observational data sets either lack controls, or if controls existed, treatment status was not randomly assigned, which means that unvaccinated people differ from vaccinated people in multiple dimensions besides vaccination status. Therefore, it is wrong to attribute all observed differences between the two groups to vaccination only.

Let's teleport back to the first part of 2021, weeks after the mass vaccination campaign commenced, when the first observational study appeared in print. For the sake of argument, let's say the first analysis showed a VE of 50%. How do we know whether this estimate is to be believed since the people who got vaccinated were clearly different from those who didn't? The honest answer should be no one knows because there is no ground truth in an observational study.

What circumstantial evidence do we have? The only breadcrumbs are interim analysis results from randomized clinical trials that produced VE of 90%+. We face a gnarly problem because our hypothetical observational study led to a VE estimate of 50%. One of the numbers is not like the other; they cannot both be correct. But which study is wrong?

Not surprisingly, most would give more credence to the RCT results, since RCTs are considered the gold standard of medical research. Therefore, since our observational study came in much lower, we'd go back to the drawing board, and massage the dataset some more... until the estimated VE is closer to 90%, making it more credible. The additional data massaging is justified by best practices - we are simply addressing residual confounding bias.

(It is important to realize that randomized experiments can be analyzed in a straightforward, standardized manner but observational studies rely on statistical adjustments that involve subjective judgment from researchers. Analysts try to guess what biases exist in the data, and device ways of correcting for them. It's an iterative process with limited guardrails.)

To make sure you get what's going on, think about what happens if the first analysis of an observational dataset leads to a VE value of 90%. This result would be immediately accepted. Nevertheless, it's not clear that this research team did a better job adjusting for bias than the previous team who came up with 50%.

Since the RCT result was the only piece of available evidence when the first observational study showed up, it became a filter for all subsequent observational studies. Any observational study that produces a number close to 90% feels comfortable, and any study that shows a number far from 90% feels "wrong". Such an editorial process directly triggers the file drawer effect.

***

I don't know how we landed on this stupid state of affairs. Using an observational study to "confirm" an RCT result - the gold standard - is like asking a C student to grade an A student. After the teacher has already given the A student a top grade, what additional information is gleaned by having a C student grade the A student's exam?

What's happening is even more dubious. The C student is not grading the same exam that the teacher saw - the C student is asked to grade a different exam submitted by the A student. By this, I mean: the observational studies are different from the RCTs in meaningful ways, e.g. timing of vaccinations, incidence of Covid-19, types of people eligible for vaccination, residence of patients, no placebo shots... There is scant justification for assuming that the observational studies should produce VE values in the same ballpark as the RCTs!

When another observational study comes out proclaiming 70-90% VE, it doesn't mean much. It just tells me that the research team has selected a set of adjustments so that the VE estimate lands in the zone that is considered acceptable for publication, i.e. it falls in the vicinity of the RCT result.

 

Lurking Variables

Another way in which we can get fooled by the consistency of results is via unknown or unexplored sources of bias. All observational studies can only control for factors for which there are measurements. I haven't encountered yet an observational study of Covid-19 vaccines in which the researchers collected their own data. The current practice is to pull data from pre-existing, government databases. So the variables available are typically limited to basic demographics (age, gender, etc.) or health-related data (prior health concerns, healthcare usage, etc.). Important factors such as attitudes toward freedom and government authority, risk tolerance and exposure to the virus, are not measured, and not adjusted for.

If key sources of bias are not adjusted for, they could explain why the results are so consistent among the subgroups; each such result contains residual confounding from the missing variables.

The missing variable may be a common cause of both vaccination status and infection outcome, for example, people who are generally more health conscious and healthier pre-Covid. They are both more likely to get vaccinated and less likely to get infected (regardless of vaccination status). Since the government databases have no labels for this type of people, there is no way to correct this bias. It is delusional to think that dumping age and gender variables into a regression equation properly adjusted for such a bias. There are health-conscious people in every agexgender segment! In each such demographic segment, vaccination status is still confounded with health-seeking status.

 

Multiple Comparisons

When so many analyses are performed using so many metrics, the best practice is to adjust for multiple comparisons. The general idea is that if one screens a lot of metrics, a few of them will accidentally show statistical significance, and those results are highly likely to be spurious. In other words, without adjustment, traditional statistical methods underestimate the degree of variability in the outcomes. That is to say, results appear more consistent than they are. Yet, most of these vaccine studies sidestep this issue.

I'd be shocked if elementary medical statistics courses don't cover the problem of multiple comparisons. Practitioners in this discipline seem to think that fishing for significance is fine so long as they pre-specify all their intended analyses. Actually, pre-registration does not solve the problem of multiple comparisons at all, unless the pre-registered statistical analysis explicitly outlines a strategy for dealing with it. (Unfortunately, the randomized trials also pre-registered multiple comparisons without correction.)

 

Poorly Defined Metrics

Another reason for consistent results across many analyses is a poorly chosen scale for one's outcome metric. An analogy to grade inflation in schools is telling. American schools has a grade-point average (GPA) typically defined on a scale of 0-4, 4 being grade A. Due to the grade inflation trend, most of the grades given out are As so in reality, the majority of the scale 0-3.5 is basically empty, with almost all students squeezed into the 3.5-4.0 range. Of course, all students look more or less the same.

I think something like this is at play with the relative ratio scales used to measure vaccines. I think an ineffective vaccine will show a VE substantively higher than 0% so the grading scale is compressed just like in schools.

***

In this post, I have offered five possible reasons why every research study of Covid-19 vaccines seems to offer similar effectiveness estimates, and why there appears to be little or no variability when aspects of the methodology are altered. As a statistician who have analyzed a lot of human data, I find it least likely that the reason for the consistency is that these vaccines are like a law of nature, such an overwhelming force that flattens all human variability.

Is this data science professor a victim or a villain?

Apparently, some secretive entity is trying to maximally embarrass Forbes magazine as much as possible. One by one, they are exposing people on Forbes' 30 under 30 or 40 under 40 list of young entrepreneurs as fraudsters. Elizabeth Holmes has already been found guilty of fraud in her medical tech startup. Sam Bankman-Fried is being sued for running a type of Ponzi scheme in his crypto startup. And now, Charlie Javice is being sued by JPMorgan for faking customer lists in her college financial aid app startup (named Frank).

According to the Wall Street Journal (link with paywall), an unnamed data science professor played a role in this fraud, and that definitely caught my attention.

The unnamed professor, who was paid $18,000, used computer-generated information to show Frank’s purported user base, including details like names, birthdays and schools they attended, the suit alleged...“Our plan was to sample first name and last name independently and then ensure none of the sampled names are real,” the suit alleges the professor wrote to Ms. Javice.

This sounds very bad. Apparently, JPMorgan alleged that about 90% of the data were faked.

However, I don't think we can read from this excerpt whether the professor has also been duped, or the professor was part of the con. It could be the case that Javice contracted the professor to generate simulated data, supposedly for some legitimate purpose.

The other reason this case strikes a chord with me is that many of the emerging data science/AI technologies can easily be exploited to deceive and hurt people, and there does not appear to be much serious discussion of this problem.

 

P.S. [1/19/2023] My friend Mark P. sent me a note saying that some people on Twitter who has read the lawsuit learned that Excel is featured in it. Apparently, JP Morgan got suspicious when they received an Excel spreadsheet with the customer data, which cut off at ~1 million rows, which is the row limit for Excel files.

I have to say I don't really understand this point because I'd have thought that their IT people didn't realize that 4 million names don't fit into an Excel spreadsheet; I wouldn't have immediately assumed they had fewer customers than they claimed.

So what if rule-breakers are unvaccinated

In the last post on the Covid-19 vaccine and traffic accidents study (link), I reviewed the analysis methodology: I found it hard to believe the vaccinated and unvaccinated groups differ only by their vaccination status, even after “adjustments”, and thus I am not convinced by their causal interpretation.

In this post, I examine a few issues.

Right at the start, the research team proclaimed:

The proximate causes of most crashes are human behaviors including speeding, inattention, tailgating, impairment, improper passing, disobeying a signal, failing to yield right-of-way, or other infractions.

This assertion is pivotal to the research conclusion, which they exploited by using involvement in traffic accidents as a proxy for rule-breaking behavior on the road. The researchers speculated that an underlying trait of rule-breaking is the common cause of (a) a higher risk of traffic accidents and (b) more vaccine hesitancy which results in a lower chance of being vaccinated.

The causal diagram – even if true – can have few public policy implications. It explains a plausible self-selection bias in the unvaccinated group (inherent rule-breaking personality). It may suggest that if governments successfully “cure” this bias, then we’d simultaneously observe not just higher vaccination rates but also a reduction in traffic accidents, other traffic violations, other crimes, absenteeism in schools, fare evasion in public transport, tax evasion, etc. But solving general unruliness appears to me a much harder problem than solving vaccine hesitancy!

The claim that most traffic accidents are driver-caused is supposedly supported by a third-party reference but that study tallies only traffic accidents involving fatalities (which comprised fewer than 0.2% of the outcomes in this study), and even so, about half of the documented fatal accidents occurred under “normal” conditions, without any rule-breaking.

The causal proposal is further weakened by linking individuals to traffic accidents even if they were pedestrians or passengers, rather than drivers. These people – who could not have caused crashes through undesirable behavior – accounted for almost 60% of all outcomes.

Imagine a drugged out but unvaccinated driver carrying one passenger in the car ran a red light, and hit and killed a pedestrian. All three individuals are counted as involved in traffic accidents. The study authors would have concluded that the unvaccinated driver would not have crashed the vehicle if s/he had been vaccinated. By contrast, if the pedestrian was unvaccinated, then the study authors would have us believe that s/he would not be dead if vaccinated, regardless of whether the driver was vaccinated!

It’s a mess. It’s easier to avoid such a mistake if one collected the data through shoe leather.

***

One factor that drives vaccination behavior has received scant attention – risk tolerance. It’s well known, and not just among economists or psychologists, that humans have varying levels of risk-seeking or risk-averse behavior. Much of the insurance and gambling/gaming industry is built upon such heterogeneity. We also know that the measured risk of Covid-19 infection or case severity depends substantially on key demographic factors such as age, gender, occupation, and prior comorbidities. So it should be obvious that propensity to want the Covid-19 vaccine should vary with (a) predictable risk of infection and/or case severity (b) individual level of risk aversion and (c) individual’s assessment of probability of exposure, including the interaction between these factors.

The public-health narrative tends to adopt an axiom that everyone is alike, and that may be its biggest failure. As noted in the prior blog, the peer reviewers and the study’s researchers failed, by neglecting the most obvious proxies for the above factors – prior traffic accidents, and prior healthcare usage. They have no excuse for excluding these factors because the former was computed for the follow-up period while the latter was used in an exploratory matching analysis. The research finidng will be seen in a new light if it turns out that the unvaccinated group had been involved in more traffic accidents prior to the study period, for example.

***

All over the paper, risk is given in the form x per million chance of getting into traffic accidents. For example, the risk for unvaccinated was described as 912 per million, and for vaccinated, 530 per million. These are tiny numbers made to look huge. Since there were 1.8 million unvaccinated, the ~900 per million means about 900*1.8 = 1,620 unvaccinated people were involved in accidents, while 500*9.2 = 4,600 vaccinated people were involved in accidents. In what period of time?

Glad you asked :) The study has a follow-up period of just one month (30 days)! Literally, the research only covered the month of August, 2021. They did not look at any other month. (It’s quite likely there would be some reversion to the mean over time.)

912 per million is another way of saying 0.0912%. Roughly 0.1% of unvaccinated people were involved in a traffic accident during August 2021, and roughly 0.05% of vaccinated people were involved in a traffic accident. Only 16% of the population were unvaccinated. Even if we assumed correlation is causation, and if we forcibly vaccinated everyone, the impact of such a policy is 1.8 million * (0.05%) = 900 people. It’s 900 people out of 11 million, and remember, some of these are pedestrians or passengers, not drivers. Most of these accidents have zero fatalities.

This number represents the risk in a single month, not annualized. There is no explanation in the paper as to why such a short follow-up time was applied. Perhaps it has to do with the continuing vaccination campaign, so that the number of unvaccinated – and thus potential beneficiaries – keeps declining. (For those interested, none of the main results in the study censor or remove unvaccinated people who subsequently got vaccinated during or after August 2021.)

***

As with most Covid-19 observational studies, researchers selected a start date for counting outcomes, and didn’t bother to demonstrate that their findings are invariant to the choice of such a date. In this study, the follow-up start date was set as July 31, 2021, so the follow-up period comprises the single month of August 2021.

This is a strange date on which to settle. Take a look at the case curve in Ontario:

At the end of July 2021, cases in Ontario were at a trough, and during August, Covid-19 cases were steadily growing. This entire month missed the next peak of infection, which was toward the end of the year. In each Covid-19 wave, hospitalizations and deaths lag cases. The following curve shows Covid-19 deaths in Ontario:

Thus, many of the deaths associated with cases reported in August showed up after the 30-day follow-up window (in September). We should ignore any commentary on hospitalizations and deaths - specifically, the claim that this study “validate[d] that vaccination is associated with large reductions in subsequent COVID pneumonia.”

The authors pointed to Table 3 to support the COVID pneumonia claim. There, we find a total of 5,358 cases. This number is five times higher than the hospitalization count shown in the above chart for August 2021 (31 days x < 30 per day), implying less than 20% of patients with COVID pneumonia are hospitalized. This contradicts the description by Cleveland Clinic that says "If you’re diagnosed with COVID pneumonia, it’s likely that you’ll be admitted to the hospital." (link).

What else happened during August 2021? The Ontario government started to differentiate testing policies between vaccinated and unvaccinated mid-month (link). In some settings, only unvaccinated people were subject to routine testing. The more tests, the more cases found.

What else also happened during August 2021? According to this press release, the provincial government issued a vaccine mandate for "high risk" settings, made third doses more widely available, and expanded Pfizer vaccine to younger children. These policies create selection bias in the analysis groups.

The timing issue is an endemic problem with all Covid-19 observational studies. Researchers should repeat the same analysis methodology applied to different time periods and show us the results. I have a hunch that many of these results are transient.

 

P.S. [1/11/2023] Added link to the original study

The traffic accidents study exposes the lamentable state of Covid-19 science

tldr; The recent study tying lack of vaccinations to traffic accidents illustrates everything that is wrong with the state of our peer-reviewed scientific process. The study uses data that do not capture any of the important behavioral factors driving one's vaccination status and propensity to traffic accidents, and yet draws conclusions as if the biases in the observational data have been sufficiently cured. The researchers ignores some findings that contradict their headline and which reveal shortfalls of their methodology. These inconvenient results suggest that their regression model did not adequately correct the biases. The model structure does not align with the hypothesized causal structure, which in any case is far too complex to be handled by a basic regression. Worse of all, the study foregrounds an entirely inappropriate analysis, on to which reporters latched. Peer reviewers somehow looked the other way.

Late last year, several readers prodded me to blog about a sensational study urging people to take Covid-19 vaccines in order to prevent traffic accidents (link). Indeed, I had already noticed the breathless headlines, and flagged the study as suspected “science for emergency use” (i.e., not the usual science).

Now that I’ve read the paper, I confirm the initial suspicion. The study is not frivolous, as these researchers made efforts to strengthen the evidence on a finding that is predictably controversial. Nevertheless, they fell too much in love with a headline grabber, and missed some red flags.

As with most Covid-19 observational studies, these researchers gained access to a set of government databases – vaccinations, Covid-19 cases, demographics, traffic accidents, etc., linked them together, selected a “test group” and a “control group”, and performed several statistical analyses, ranging from simple tests of proportions to regressions with simple adjustments. Reflecting the preference during pandemic times, this type of research is conducted purely remotely, in an arms-length manner, without any engagement with the persons or objects under study. It’s quintessential ivory-tower data mining, no use for shoe leather.

For this study, the researchers obtained “N=All” data from Ontario, Canada. They selected about 11 million people to include in their analyses, divided into those who have taken zero vaccine shots (“unvaccinated”) and those who have taken one or more vaccine shots (“vaccinated”). The unvaccinated group comprised only 16% of the analysis population at the time of the analysis.

The researchers chose to highlight their least convincing result, perhaps because it carries the biggest “effect”. This is the claim that “unvaccinated individuals [experienced] a 72% increased relative risk [of traffic crashes] compared with those vaccinated”. This claim orginates from a simple, unadjusted comparison of the rate of traffic accidents between the two groups.

This simple, unadjusted comparison is completely useless! It is valid only under the obviously false assumption that the only difference between the “test group” and the “control group” is their vaccination status. Nevertheless, reporters latched onto it like sticky glue. I like to use the term “XYopia” (i.e. X-Y myopia) to describe the fallacy of pretending that the observed outcome Y (traffic accidents) is affected only by the offered explainer X (vaccinations) and nothing else.

In fact, the observed difference in traffic accident rates could be partially or wholly due to any number of other factors. After all, this type of research study is an exercise in data mining, not a carefully designed clinical trial. In every province and country, the unvaccinated group is expected to vary from the vaccinated group, not just in their vaccination status but due to self-selection and local, discriminatory vaccination policies. Thus, any unadjusted analysis ignoring other factors is pure garbage.

Why did the researchers let this happen? It’s not like they can’t smell the stench from a mile away. This is elementary stuff taught in the first lecture on observational studies. The paper actually included several adjusted analyses. Maybe they will argue that the simple analysis was “pre-registered”, and thus according to the norms of scientific publishing, they are “obligated” to headline it. The protocol is not published so we don't know. If true, this situation exposes the Achille’s heel of using “pre-registration” to preempt bad science – since patently absurd statistical methods could be pre-approved. (Besides, in many other Covid-19 studies, including trials, the protocols were continuously "revised" up to the time of analysis, rendering pre-registration toothless.)

After adjustment, the relative risk increase dropped to about 50% (the adjustment is insufficient, as indicated below).

***

The researchers are well aware that their finding would be controversial, obviously a prime example of correlation, not necessarily causation. This is also where "causation creep" shows up. Just like the majority of such studies, the authors clearly state that "correlation is not causation", but their conclusion - "Together, the findings suggest that unvaccinated adults need to be careful indoors with other people and outside with surrounding traffic" - makes sense only under a causal interpretation of the observed correlation.

Think about the situation faced by all research on observational data. If the finding is merely an interesting correlation, there is no reason to publish it, as the correlation could be spurious. The only studies that could get published are the ones in which the researchers somehow turn that observed correlation into causation. What's strange and wrong in my opinion is the declaration that they have found only a correlation when they have convinced themselves (and peer reviewers) that they have offered sufficient evidence of causality. If that's what they believe, they should own it and say it clearly.

To strengthen their own conviction of causality, the researchers sliced and diced the data some more, and found a similar signal almost everywhere. Instead of ringing alarm bells, such unlikely consistency is interpreted as confirming the aggregate result. But the signal isn’t “everywhere”, only everywhere they looked. If an overlooked factor was driving the aggregate result, it may well drive all the subgroup analyses, with the neglected factor cutting across all the known subgroups.

For example, in Table 2, the analysts replicated the simple unadjusted comparison of rates for a variety of subgroups, such as males, younger or older age, people with cancer, etc. We learn that among those older than 65 years old, those unvaccinated have a 30% lower risk of traffic accidents than those who are vaccinated. (This finding, just like the other findings, assumes all else is equal, which is obviously false.) Applying the same reasoning these authors used to interpret the 50% overall percentage increase in risk, we’d have to advise Ontario residents above 65 years old against getting the Covid-19 vaccine as doing so may make them more vulnerable to traffic accidents! This effect remains even after adjustment.

Next, in Table 3, the researchers performed the simple comparison of vaccinated vs. unvaccinated on subsidiary outcomes. One such outcome was involvement as pedestrian (rather than driver or passenger). Amusingly, being unvaccinated increased the risk of getting hit by vehicles by 40% (p = 0.00). Moreover, not getting the vaccine more than doubled the risk of traffic accidents *at night*.

Any attempt to explain away these inconvenient findings will involve invoking some other factors e.g. maybe unvaccinated people are more likely to have a night life – such theorizing does not rescue the analytical model but merely proves that it failed to account for all relevant factors.

The wayward results were disclosed in the paper – the research team chose to look the other way, focusing on the outcomes that support their headline-grabbing conclusion. But these results demonstrate that the "adjustments" applied have failed to cure the selection biases in the observational data.

***

It comes as little surprise that the simple adjustments do not cure the selection biases. (And when such biases are not cured, they could infect any analysis.) This problem is endemic in the Covid-19 literature. Most studies - including this one - rely on basic regression models that include just main effects of various demographic variables (age, gender, location, etc.). Very few of these studies publish the actual models - almost never do we see any tables of coefficient estimates or goodness of fit statistics. Almost no one discusses the causal structure associated with the structure of their regressions. Nevertheless, they all proceed as if their adjusted models have completely cured any selection biases.

The regression model in the traffic accidents study accounted for "baseline demographic and diagnostic predictors", which are not explicitly listed. Presumably they contain the items in Table 2: age (<40, 40-64, >65), gender, urban/rural, socioeconomic status (high, medium, low), prior alcohol misuse, prior sleep apnea, prior diabetes, prior depression, prior dementia, prior hypertension, prior cancer, prior Covid-19 infection.

Missing from this list is the most obvious one: prior traffic accidents. Another obvious one is prior vaccinations. I'd also include prior traffic violations. Yet another relevant factor is prior hospitalizations or hospital contacts. I'm not sure how peer reviewers missed all these.

This last factor is clearly important - but most of the Covid-19 researchers make a ridiculous decision - that is, they excluded people with recent hospital contacts, which improperly injects a healthy person bias into all such studies. This factor should not be used as an exclusion criterion but should be an adjustment variable.

The study's appendix includes a very telling causal graph:

I'm not going to adjudicate as to whether this diagram properly captures the complex relationships between these factors, nor whether it includes all relevant factors. Just focus on the white nodes - these are the only factors/outcomes that have real-world measurements, and are represented in the regression model. Everything else is not directly observable.

The regression model ignores all the unmeasured quantities so it is inconsistent with the above diagram. And yet, they assert that all biases have been cured. Alright - they didn't really claim all biases have been cured. In fact, they compiled a long list of factors that they knowingly ignored. In describing the "limitations" of the study, they listed the following factors: distrust of government, belief in freedom, misconception of everyday risks, faith in natural protection, antipathy toward regulation, chronic poverty, exposure to misinformation, insufficient resources, other personal beliefs, political identity, negative past experiences, limited health literacy, social networks, amount of driving, vehicle factors (speed, spacing, configuration, location, weather, distance driven), access to care, risk compensation, non-reported crashes, etc.

The researchers' stance is that since they don't have data for these factors, they are left as homework exercises for future research. That regrettably is normal research practice: even though many important factors are ignored, the study is still publishable since the researchers acknowledge the "limitations". It's like an investment banker disclosing all the reasons why a tech startup would tank, while still selling the IPO stock fervently. Here is a sample from Twitter's 2013 IPO that is good for giggles:

• "Our products and services may contain undetected software errors, which could harm our business and operating results."
• "We rely on assumptions and estimates to calculate certain of our key metrics, and real or perceived inaccuracies in such metrics may harm our reputation and negatively affect our business."
• "We have incurred significant operating losses in the past, and we may not be able to achieve or subsequently maintain profitability."
• "If we fail to grow our user base, or if user engagement or ad engagement on our platform decline, our revenue, business and operating results may be harmed."
• "If we fail to effectively manage our growth, our business and operating results could be harmed."

Maybe it's just me - if I believed those risk factors (plus many others), I wouldn't buy this stock. But of course, I wouldn't buy any tech stocks since they all use similar language.

If had read the limitations of the traffic accidents study first, I'd have saved a lot of time by not reading the study.

 

P.S. This post has run too long, and I'll post the second part next week.