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

What's smelling fishy? Maybe your data

In the comments to the previous post, a PhD student asked for general advice on testing data for irregularities. This topic merits a separate post, indeed multiple posts.

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Here are some initial thoughts:

1. Your data is guilty until proven innocent

2. The top N rows of your data may be false friends

3. With experience, you develop an intuitive feel for the common types of problems to look for

4. Look for problems in slices of the data, because problems are not randomly distributed throughout your dataset

5. Avoid inferring metadata from the data - find the metadata or ask the data collector

6. Seek contradicting statistics: e.g. if A and B have these values, then it's impossible for C to have this value

7. Pushing bad data into your analysis pipeline, and then fixing problems as they surface does not save time; on the contrary, it will cost you much more time

8. Many problems are caused by data collectors who have no knowledge of how the collected data would be used in the future by data analysts

Better late than never

Quick quiz. Who wrote this?

I did not test the data for irregularities, which after this painful lesson, I will start doing regularly.

Of course, you won't know. But which of the following people is the most likely to have said such a thing?

A) A Stat 101 student

B) A data scientist working in industry during the first year of employment

C) A graduate student research assistant

D) An assistant professor in the publish-or-perish game

E) A senior tenured professor with multiple best-selling books and tens of thousands of citations

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If you think the least likely is the most likely, then you'd be right. The answer is (E).

The person who said the sentence (in 2021) is Dan Ariely, currently a Duke professor of economics but probably known to my readers as author of a series of best-sellers in behavioral economics, starting with Predictably Irrational. (You can find the quotation in this PDF.)

Andrew has documented a series of scandals in which several of his seminal studies have been called into question. The latest one involves data obtained from an insurance company by Ariely. He now claims to have no role in collecting, and processing the data.

Neither did the people who uncovered this potential research fraud. Hence, the ability to suss out data problems does not require first-hand involvement in collecting or processing data.

To read about how the fraud was detected, see here.

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Next time you hear about a publication in a "peer-reviewed" scholarly journal, think about this case. It is entirely possible to publish data analysis in a peer-reviewed journal without "testing the data for irregularities". In fact, researchers with hundreds of peer-reviewed publications may have never once tested data for irregularities! Better late than never, right?

 

P.S. (1) If you need something light for the holidays, here is an advice column Andrew, hmm, wrote for the WSJ.

(2) One of Ariely's best-sellers is "The Honest Truth about Dishonesty". He is an expert on honesty.

 

Thirty percent unvaccinated in healthcare: less than meets the eye

When I saw this "news" on my Twitter feed, I knew I have to write a blog post about validity of research results. There is an ongoing plague in which science reporters broadcast top-line results without ever checking the underlying papers - which disclose how limited most of these results really are.

The most important words in the above excerpt is not that 30 percent of U.S. hospital-based healthcare workers are still unvaccinated - they are "for whom data on vaccination status was available".

The published paper is here. I'll summarize what you'll learn from it.

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The report covers only 40% of U.S. hospital-based healthcare workers. The source is a database in which hospitals (sometimes through the state health departments) voluntarily enter aggregate data.

About half of the hospitals in the U.S. contribute data to this database. Another 10% of hospitals were dropped because of exclusions.

"Psychiatric, rehabilitation, and religious non-medical facilities were excluded." I really don't know why.

Also, hospitals for which "total HCP" (healthcare personnel) or "HCP vaccination" fields are missing or zero are excluded. The confounding of missing and zero is a common database problem. Does zero mean zero or missing? By using this exclusion, the analysts made the assumption that zero means missing, and not zero.

Yet another exclusion applies when unvaccinated personnel and fully vaccinated personnel summed to less than 75% of the total number of HCP. This means they excluded any hospital in which a significant number of HCPs have taken one shot or have taken two shots but not reached 14 days. I really have no idea why this exclusion is needed.

P.S. On second thought, I think this provision is associated with the desire to put "unvaccinated" into the headline instead of "not fully vaccinated". However, when such an exclusion has been added, then the first part of the sentence should really say 30% of hospital-based healthcare personnel excluding those who are partially vaccinated. So, no, I don't like this exclusion, and the headline is inaccurate.

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What is the implication of exclusions? It causes the study findings to become less generalizable. It also confuses readers. When people read "30% of hospital-based healthcare personnel are unvaccinated", they think 30% of all such personnel. When they do that, they made the implicit assumption of no non-response bias, i.e. the hospitals excluded from the study are the same as those included.

Ex ante, we know that assumption to be false. If that assumption held, then there would be no need to exclude hospitals in the first place.

If excluded hospitals (including those who chose not to participate) are different from included ones, then the study finding can only apply to included hospitals, which represent less than half of total hospitals. In statistics, we say exclusions reduce the "validity" of results.

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Many statisticians, including myself, prefer to make educated guesses to close the gap. We'd like our overall finding to generalize to the whole country. We'd therefore need to predict what answer we would see from the excluded hospitals should we have their data. This prediction can use data from the included hospitals with appropriate adjustments.

A key to such a prediction is to find differences between the excluded and included hospitals. According to the paper, excluded hospitals are less likely to be critical access hospitals, more likely to be non-rural, and more likely to be larger in size. (The implication of this last factor is that the 40% of hospitals represent less than 40% of all hospital-based HCPs.) The authors stated that the first two factors are associated with higher vaccination rates, and so the excluded hospitals may in fact have higher rates than those included.

Here is where you find heated debates between statisticians. Some argue that any such prediction injects subjectivity into the analysis. I take the other side of this argument. Not injecting subjectivity is a mirage. When you don't make adjustments like these, your results assume no adjustments are necessary, which is to assume no bias exists, and allow readers to implicitly extend biased results to the entire population. The adjustments may fail entirely or partially but I don't think the adjusted results are any worse than the unadjusted ones.

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The adverse impact of hidden biases in the dataset is easily missed.

Consider the following sentence from the paper:

Coverage was higher among HCP working in facilities located in metropolitan counties (71.0%; 95% CI: 70.9, 71.0), followed by HCP working in facilities located in rural counties (65.1%; 95% CI: 64.8, 65.3), and HCP working in non−metropolitan urban counties (63.3%; 95% CI: 63.1, 63.5).

We know that rural hospitals have a higher response rate than urban hospitals. Responders are likely to be different from non-responders. So we don't know whether vaccination rate by degree of urbanicity would be in that precise order were we to have complete data.

The same problem applies to every conclusion of the study, e.g. children's hospitals have higher vaccination rates. In some cases, the connections are not obvious. (Children's hospitals are not likely to be equally distributed in urban and rural areas.)

 

Further adventures of case-counting windows

If it's not already clear, observational data is a great playground for statisticians. We sniff out where biases are hiding, and we devise methods to correct such biases. It's a lot of fun. It's also frustrating - because there are endless ways to make adjustments.

In today's post, I examine a couple of curious observations made by the Israeli researchers when they analyzed the data from vaccine boosters (link).

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The researchers shrank the follow-up window when counting severe cases (relative to counting cases)

This decision surprised me because severe cases are a fraction of all cases so I'd want to have a longer counting window, not a shorter one.

Recall that in the analysis of cases, the Israel booster real-world study pulled data from the national database for the month of August. Because of a case-counting window that starts 12 days after the booster shot, in effect, the study only counts cases from August 11 to August 30. Most people did not get the booster on July 31st, and so the average follow-up time is probably around 10 days. (See the previous post for more.)

For severe cases, the case-counting window shrank by 4 days, as the researchers stopped counting on August 26 instead of August 30. Thus, the average follow-up time for severe illness is around 6 days. You're right - protection against severe illness was shown for less than a week.

Here is a direct quote that explains why the case-counting window was shortened for severe cases relative to all cases:

In order to minimize the problem of censoring, the rate of severe illness was calculated on the basis of cases that had been confirmed on or before August 26, 2021. This schedule was adopted to allow for a week of follow-up (until the date when we extracted the data) for determining whether severe illness had developed.

In the Appendix, the researchers offered the following chart as supporting evidence:

This chart shows the lag between testing positive and the onset of severe illness for Covid-19 cases between November and March 2021 (conditional on people subsequently getting severely ill). The median lag is 4 days, meaning among those who eventually got severely ill, half got severely ill within 4 days of testing positive, and half got severely ill after 4 days (up to almost 30 days).

I believe the logic is that for anyone who got sick in the final 4 days of August and became severely ill, the onset of severe illness would have taken place after the data cutoff for this study.

Consider the following implications:

• According to the chart above, half of the past patients took over 4 days and up to 30 days to develop severe illness. If we want to capture all severe cases, we ought to extend the follow-up period to at least 30 days - it should be 60 days if we use a one-month cohort. The methodology based on median lag time would capture only half of the severe cases.

 

• Think about the severe cases that occurred between Aug 26 and Aug 30. These severe cases are connected with infections that occurred prior to August 26, most likely during August. They are excluded from the analysis. All of these severe cases should count. The severe cases that happened on the first 4 days should be dropped, if we use their logic. (Note that the infection rate was skyrocketing during August.)

 

• Now think about someone who took the booster shot on August 16. If this person became severely ill on August 26, the severe case is not counted. But this severe case represents a lag time of 10 days from detection of infection, which according to the chart above, happens more than 10% of the time. This issue arises because the case-counting window is given a fixed ending date regardless of when the booster was administered.

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The researchers disclosed they faced an incurable imbalance problem.

Part of the paper's Appendix is devoted to alternative analyses, one of which is a matching study. I discussed examples of matching studies before (Mayo Clinic, and Clalit). Unfortunately, this disclosure did not contain enough details to evaluate the quality of matching.

The following statement caught my eye: "Due to the very small number of severe cases, and the high censoring proportion, calculation for severe COVID-19 was not possible."

In my comments on the Clalit study (link), I mentioned a limitation of matching studies: if selection bias is severe, it may be hard to find acceptable matches, leading to dropping many unmatched cases ("high censoring proportion"). In this case, the matched population ended up being much younger than the vaccinated population.

In the Israeli booster study, the researchers attempted to find one person who hasn't taken the booster to match with each person who took the booster. Matching variables are the usual suspects like age group, second-dose date and so on. They appear to be saying that they failed to find adequate matches for a large proportion of the booster group. This is a sign of incurable covariate imbalance. This also suggests that those regression adjustments used in the main analysis are insufficient.