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

Ethical dilemmas poll: results post

Update on 8-29-2023

Last week, I put up a poll that asks users what they would do if faced with some ethical dilemmas that arise on the business side of data science. I'm presenting the first set of results here. I'm guessing the responses have stabilized but will provide further updates below should the trends shift.

Case Study 1

Is it acceptable for BestHotels.com to present fake statistics to influence users?

A. Yes (8%)

B. No (87%)

C. I don't care (5%)

 

Case Study 2

Has AnyVoice done enough to mitigate such scams?

A. Yes (18%)

B. No (73%)

C. I don't care (9%)

 

Case Study 3

Should ZT&C launch the downgrade campaign?

A. Yes (27%)

B. No (42%)

C. I don't care (31%)

 

Case Study 4

Should banks be allowed to sell such customer data?

A. Yes (8%)

B. No (92%)

C. I don't care (0%)

 

Case Study 5

A. Yes (66%)

B. No (30%)

C. I don't care (2%)

 

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What do I make of these results?

First the limitations. They reflect the biases of my blog's readers. Also, these issues are worthy of a substantive debate that goes beyond a poll. I chose scenarios that I think are not clear-cut, allowing arguments from either side; the poll format forces readers to pick a side, and it appears on average each question (except one) has a definitely more popular position.

The most lop-sided response came for Scenario #4 in which data scientists purchase bank account data to develop "personalized" pricing. Over 90% of respondents don't want banks to sell their data for this purpose. This is also the only scenario in which almost everyone had an opinion!

People in the business already know that this scenario has already happened, and I am not aware that any American government agency has bothered to ask citizens whether they condone this practice. One agency did intervene to stop a merger between Visa and one of the key vendors of such data but that action isn't a pushback against selling bank account data.

Food for thought: can these data science models be justified because they advance social justice? One could argue that the pricing tool would hike prices on those who can afford them while lowering prices on those who can't.

***

Scenario #3 is also an example of personalized pricing: here, the data scientists create models that determine whether broadband subscribers are paying too little or too much. The responses are roughly split in three: respondents who have no opinion; those who want to notify premium subscribers that they can save money by downgrading their plans; and those who think the company should let the subscribers stay in their plans.

In this case, the business has all the usage data it needs to build the model, unlike in Scenario #4 when the best data for the job must be acquired from third parties. In Scenario #4, the business adjusts pricing for everyone while the overall change leaves the business with more revenues. In Scenario #3, the business definitely takes the action that increases its revenues, and is debating the other action that suppresses revenues.

***

Here is the link to the poll.

 

If it's an RCT, it can be trusted

I've written often about the problems with conducting observational studies. We like to hold up randomized controlled trials (RCTs) as the "gold standard," and if a study is described as an RCT, and especially if its design is pre-registered, we don't ask many questions.

This point of view is becoming unsustainable, based on a recent Nature article.

The gist of the article is that experts now believe at least one out of every four RCTs contain so many problems that their findings should be ignored, leaving the possibility also that some of these RCTs may be entirely fake. In coming to this conclusion, these experts sought and received the underlying individual-level datasets.

These problematic or fake RCTs make their way to systematic reviews (aka meta-analyses), and throught those, they sometimes influence medical practice. Systematic reviews are summary articles that weigh evidence from all studies on a given topic, e.g. whether sugar helps reduce death after head injuries.

In a particularly egregious example, a late Japanese bone-health researcher has had over 100 studies retracted due to fraud, but his papers have appeared in 88 different systematic reviews, half of which would have arrived at a different conclusion if his studies were omitted.

Besides, there is no universal requirement for authors of systematic reviews to revise their analyses should included studies be later retracted. What a mess!

One researcher estimated 20-30 percent of the papers included in systematic reviews in women’s health are suspect. Even when the authors of these systematic reviews have been alerted to the retracted studies, many have ignored pleas to update their findings.

When editors reject studies because of data problems from one journal, the same studies almost always eventually get published in a different journal, “sometimes with different data to those submitted [to the first journal].”

Fixing the RCT problem requires a cultural shift, which does not seem to be forthcoming.

***

The Nature article catalogs a number of objections to research that exposes RCT fraud. Here is a list:

• Privacy concerns of releasing individual-level data
• Participation agreements that do not explicitly include the right to share data
• The logistics of archiving the datasets
• The effort is not worth their time
• The potential harm of false positives
• Ethical concerns related to excluding studies, e.g. wasting the participants' time

Efforts to mandate data sharing have so far been thwarted.

***

Sad to say, the proportion of bad or fake RCTs is substantially higher than 25%. How do I know?

One expert examined over 500 RCTs, and only successfully obtained the individual-level datasets from 150 (30%). In the 30% with detailed data, he found serious problems with 25% of them.

He also looked for problems in the other 70% of the studies, but could only find issues in 1 or 2 percent of them. Paradoxically, this suggests data non-disclosure is positively correlated with trust. But not really. This result points to the fact that typical data summaries in publications hide major problems, including fake data. There isn't much the expert could have done to verify the study findings when the underlying data were not made available. I encountered this issue frequently when looking at Covid-19 vaccine studies.

If we generalize the 25% fraud from studies with data disclosure to those without, then we could conclude that overall 25% of RCTs are suspect. This conclusion assumes that whether the researchers agreed to disclose data is independent of whether their studies are fraudulent. I don't like this assumption. A more sensible assumption is that fraudulent researchers are highly unlikely to disclose their data. Thus, among the studies that don't disclose their data, we should expect a higher proportion of fraud.

Observational studies that don't include everyone intended to receive the treatment

Today, I return to the Clalit booster study. I’ve written three prior posts about the study, which was the catalyst for regulatory approval of booster shots of mRNA vaccines for Covid-19 at the turn of 2022. In the first post, I showed how the methodology - common among Covid-19 vaccine studies - contains obvious biases that researchers and their peer reviewers overlooked. (link) The booster study featured a further unexplained wrinkle – some subjects are excluded after their infection status is known (link). In a third post, I developed a sports analogy to ponder what kind of effects such analytical procedures may have on the results.

This post describes further obvious biases in the study design. There are two classes of biases that affect observational studies in which we cannot randomly apply treatment to subjects. The first class of biases occurs when the two treatment groups are not statistically identical, except for the presence or absence of treatment. The second class of biases occurs when the study population does not look like the population to which the treatment if approved would be applied.

As explained in the first post, this study is unusual in that 90% of the study population appeared first in the no-booster group and later in the booster group. Thus, if we investigate covariate balance in the usual way, the two groups would look close to identical.

So the more interesting question is whether the study population represents people to whom Clalit intends to promote booster shots should they be approved. It’s tough to answer this question without access to the data. We can address a slightly different question: is the study population a random sample of Israelis 50 years old and above?

The answer is most likely no. According to OurWorldinData, the proportion of Israelis 50 year old and above who have received at least one booster dose during the study’s time frame was between 61-80%. And yet the study reported that 90% of the subjects got booster shots during the study period. So, the study population had greater inclination to take the booster shot than the general population.

In fact, fast forward to April 2022, seven months after the study ended, and the last month for which OurWorldinData compiled data, and we learn that the proportion of 50+ year old who have received at least one booster shot was stuck at 73-86 percent, still below the 90% recorded in the study.

***

Looking at the list of exclusions from these types of studies is highly informative. The key question to ask is whether people excluded from these studies will also be excluded from the rollout of the booster. Seemingly the answer is no – the booster will be recommended for essentially everyone.

This practice makes little sense to me. If the excluded people will be given boosters, why should they be excluded from the analysis?

To make this more concrete, here’s the first exclusion criterion: anyone who have ever been infected with Covid-19 prior to the study start date. I have never heard a public health official say don’t take boosters if you had been infected before; quite the opposite – they usually claim that prior infection does not confer immunity, and recommend prior infected to take the boosters.

What might be the effect of removing prior infected? If the public health claim is correct, then prior infection does not offer extra protection to this subgroup, and therefore including them doesn’t affect the effect of the booster shot. As a subgroup, those with prior infection may look different from those without, changing the baseline infection rate but that's not a reason to exclude. If the public health claim is false, that is to say, prior infection does confer some immunity, then any effect of the booster would be attenuated in this subgroup, and excluding them improves the reported result.

Another exclusion criterion involves those whose second vaccine shot (in the original two-shot Pfizer regime) was administered fewer than 5 months from the start of the study period. Once the booster is approved, is there any enforcement of this “rule”? Are people forced to wait at least 5 months before getting the booster?

Exclusions are always present in these studies, and not enough attention has been paid to the biases that exclusions create. Excluding prior infections mean only people without prior infections are in the study. This subset includes people who are health-seeking, and those who follow non-vaccine mitigation measures seriously (masks, distancing, stay home, etc.). Meanwhile, those who ignore mitigation measures and take risks are more likely to get infected, and thus get kicked out of the study.

The other exclusion also directly inserts a bias into the study – as it selects people who are less vaccine hesitant and thus take their vaccine shots earlier rather than later.

A sports analogy for data processing rules

I'm been mulling over how to explain the potential impact of strange data processing procedures used in the observational studies of Covid-19 vaccines. These are by no means standard operating procedures.

And I think I've landed on one explanation that is tantalizing.

***

Imagine a football (soccer) match that is tied 0-0 and heading into overtime. Overtime is a 30-minute affair, played through, and not sudden death. The overtime period is divded into two 15-minute halves with a short break in the middle.

That is the standard operating procedure.

***

Now, we are going to change the rulebook.

The first additional rule is that any goal scored in the first 10 minutes of overtime doesn't count. This rule is inspired the "case counting window" used in the Covid-19 vaccine studies. We're justifying it because players need time to get back to their optimal condition after the exhausting 90-minute regulation time. Therefore, it is not fair to count goals scored at the start of overtime.

The second additional rule is that any goal scored in the first 10 minutes of overtime by the visiting team doesn't count but those scored by the home team counts. How should I justify this rule? Well, to establish the need for recovery time, we take vitals of the players. The measuring machines are only installed in the home locker rooms and not the guest locker rooms, and thus, we are unable to determine if the guest players are at their optimal condition. This rule is inspired by not applying the case counting window to non-vaccinated people since we can't determine when they took the second shot (unlike the situation in clinical trials, when non-vaccinated people are given placebo shots.)

The third additional rule divides the first 10 minutes into two parts, and stipulates that if someone scores in the latter part (i.e. minutes 6-10), then they are immediately kicked out of the match, and their goal doesn't count. This rule is inspired by the special exclusion criterion disclosed in the booster study I've been discussing (link).

This third rule is complicating as it modifies the previous rules. Taken together, we have the following scenarios: for the home team, if they score in the first 5 minutes, the goal counts; if they score in minutes 6-10, the scorer is kicked out of the match, and the goal is disallowed. For the away team, if they score in the first 10 minutes, the goal is always disallowed; in addition, if the goal is scored in minutes 6-10, the scorer is ejected.

***

One can easily get lost in the details of pharmaceutical studies and lose sight of the implications of the methodologies. Transferring the context to sports helps me grasp the effects of these data processing procedures. Hope this helps you too.

PS [8-4-2023] In my haste to put down my thoughts relating to this analogy, I skipped a rule. This is a Rule #2.5. This rule says that if a goal is scored in the first 10 minutes of overtime by the visiting team, it is counted as a goal scored by the home team. In Rule #2, the away-team goal is just disallowed; in Rule #2.5, the goal is added to the home-team tally. This rule is inspired by the booster study, in which they kept people in the no-booster group for 7 days after they took the booster.

 

 

Sloppy language misleads

One of the most frustrating aspects of reading Covid-19 related publications is reading the conclusions. A summary of results is supposed to provide readers with the minimally necessary information to understand the full contents of the paper - but what we encounter is "story time": almost always, these conclusions are stated in the most general sense, ignoring all the caveats, the exclusions, the imperfections of the methodologies and analyses. They are "stories" that go far beyond the limited evidence presented.

I've been reading the Clalit study that was a major force behind the approval of the first booster shots back at the end of 2021/start of 2022. This paper made the following one-line conclusion:

Participants who received a booster at least 5 months after a second dose of BNT162b2 [i.e. Pfizer] had 90% lower mortality due to Covid-19 than participants who did not receive a booster.

Is it possible to misread this sentence? Yes, if you literally read the sentence.

***

If we know something about vaccine efficacy/effectiveness, we immediately recognize that these authors are selling the same story - that the vaccine has VE 90%, the only difference here being the outcomes are deaths attributed to Covid-19, rather than reported cases. As such, this VE is driven by the relative ratio of the death rates of the booster group vs the no booster group. They didn't use the term VE as it typically connotes cases not deaths.

A death rate is a fraction composed of two parts: people who are counted as part of the comparison group, and people within that group who died during the study period. In this post, I'll pay attention to both these parts.

From my last post, we already know one issue with the above statement. If we take any participant at the start of the study and ask whether this person is counted as part of the booster group or the no-booster group during the study, the answer, for 90% of the participants, is both. 

Since at the start of the study, 100 percent of the participants had not received the booster, and by the end of the study period (a mere 54 days), 90 percent of them got the booster, the researchers could not have divided up the study population into two distinct groups of people - each person (except the 10% who didn't get the booster during the study period) first appeared in the no-booster group, and then transitioned to the booster group.

But the concluding statement reads like the study enrolled two distinct groups of participants. This misreading is even more likely for knowledgable readers because ordinary studies, such as well-designed clinical trials, use distinct groups.

Note that I'm not criticizing the methodology up to now, I'm describing what it is, and criticizing how the language in the summary statements sends readers the wrong message.

***

The above detail may sound trivial but it has major implications. Think about the regression adjustments. As with all observational studies, researchers claim that by adding standard covariates to their regression models (age, gender, ethnicity, prior health conditions, etc.), they have corrected substantively all biases. For example, if older participants are more likely than younger ones to want the booster, rather than being assigned a treatment at random as in a randomized clinical trial, then it's possible that the age distribution in the booster group does not mirror that in the no booster group, i.e. an age bias exists.

Look at the setup here: Ninety percent of the participants appear once in the treated group and once in the not treated group. By the design of this study, there is little variation across the comparison groups in the distribution of everything, including age. If we check "covariate balance", it's balanced because the two groups are by and large identical. So this type of studies underestimates the variability of everything - which leads to p-values that are too small, and regression adjustments that are meaningless.

***

In the paper's conclusion, the phrase "participants who did not receive a booster" is incorrect in more ways. We already know almost all of them ended up getting boosters before the end of the study period, which was fewer than two months long. I have previously said that a participant transitions into the booster group when s/he takes the booster shot.

This is in fact not true. That's because this study also imposes a "case counting window," under the claim that the booster shot takes 7 days to become effective. In other words, if someone takes a booster shot, and falls ill with Covid-19 within the first 7 days, this case is not counted as a case in the booster group.

Negating this case is one thing - but this study (and many others) took another step: the case is not negated but it is counted as a case in the no-booster group!

How do they pull this off? The study design says not to transition the participants to the booster group until the 8th day after the booster shot.

So, let's review this. Each participant starts off in the no-booster group, then the person took the booster shot; this person is kept in the "no-booster" group for an additional 7 days before being moved into the "booster" group. During these 7 days, if the person gets infected or died from Covid-19, the case or death is counted as "no booster".

Remember that we can only talk about exposure time for this type of study since almost everyone is eventually exposed to both conditions. The exposure time of the "booster" group therefore excludes the first seven days after the booster while the exposure time of the "no booster" group includes the first seven days after the booster.

This is an instance of the additional bias that Lataster described in his comment on our Three Biases paper.

***

As the story goes, even the above description is inaccurate. We haven't dealt with the following puzzling disclosure:

participants who received the booster and had a confirmed case of Covid-19 within 3 days before the effective-booster date (defined as 7 days after the booster was administered) were excluded

The analysts further subdivided the seven days after the booster shot is administered into two parts: Days 1-4 and Days 5-7. Let's follow a participiant who did not have the booster at the start of the study. During the study period, this person took the booster shot. If the person got sick during Days 1-4, the person is counted as a member of the no-booster group with infection as outcome. However, if the person got sick during Days 5-7, this person is excluded from the study, i.e. not counted as part of the no-booster group, and not counted as a case. Finally, if the person did not get sick by Day 7, the person transitions to the booster group.

There is a subtle but important difference. The Days 1-4 treatment is applied to every participant, regardless of outcome. If they got the booster, they continued to be called "no booster" for seven additional days. The Days 5-7 treatment is an exclusion based on the outcome. If the person got sick, the person is removed while if the person did not get sick, the person is retained. For me, it is never acceptable to re-define treatment groups after observing the outcomes. And yet, this paper (and many others) engages in this practice.

To understand the impact of these data processing procedures, you can use the same device we used in the Three Biases paper: imagine a vaccine that is ineffective, apply the analysis, does it result in no effect, or something else?

This is a great example of why researchers must disclose the code used to process the data. It's hard to believe these special adjustments did not get the attention of reviewers. But I can think of no other way to interpret those words. (In fact, the waterfall chart in the paper confirms the exclusions.)

***

Now that you have heard how they measure outcomes and define "no booster", it's time to revisit the conclusion:

Participants who received a booster at least 5 months after a second dose of BNT162b2 [i.e. Pfizer] had 90% lower mortality due to Covid-19 than participants who did not receive a booster.

Does this sentence correctly summarize the study?

 

 

One big problem with booster studies (and observational studies of Covid19 vaccines)

I'll be writing a number of posts about observational studies of the Pfizer booster, published by the Clalit health insurer in Israel (back in December 2021), which is the primary source supporting the effectiveness of the booster shot (3rd shot). These studies provide fodder forever for classes in observational studies because (a) there are many nooks and crannies in which residual biases hid, and (b) researchers made many assertions (wrong, of course) about having corrected all biases using the simplest, most conventional methods.

This first post points out the biggest problem with such studies, which is perhaps impossible to correct.

Let's first review the basic setup of such studies. (The devil is of course in the details, and I'll dive into those in future posts.)

Each study has a well-defined start and end date. This is not a clinical trial, so no one proactively enrolls in this study. Instead, the researchers had access to databases with relevant data and extracted the study population from it.

The start date is chosen close to the launch of the booster shot in Israel, and therefore, at the start, almost everyone was in the "no booster" group. Over the course of the study, most of these same people have migrated to the "booster" group - when they took the booster. Even though the study spanned fewer than 2 months, almost everyone (90%) received the booster shot by the end date.

Here is the first thing one must recognize. This is not a typical clinical trial in which one person belongs to either the treatment group or the control group but not both. In this study, nine out of ten people featured in both the "no booster" and the "booster" groups.

So when subsequently, researchers compare the "no booster" group and the "booster" group, they talk about exposure time, rather than number of exposed. The exposure time of the "no booster" group are incurred mostly by people who eventually got the booster within the study period. This is key observation #1.

If we now hone in on an individual who got the booster shot during the study period, the entire observation time is divided into two parts: from start of study to the day of the booster ("no booster" exposure), and from the day of the booster to the end of the study ("booster" exposure). It is 100% certain that the exposure time in the "no booster" group precedes the exposure time in the "booster" group. This is key observation #2.

Moreover, observation #2 deos not depend on the date of booster, which varies by person. Since individually, each person is exposed first to "no booster" and then to "booster", collectively, the exposure time of the "no booster" group is skewed towards the start of the study period while the exposure time of the "booster" group is skewed towards the end of the study period.

What else do we know about the booster study (or, the majority of Covid vaccine studies)? These studies almost always begin during a peak infection period, which means the infection rate dropped during the study. This is key observation #3.

Together, our three observations mean that the exposure time associated with the non-booster group is skewed towards the front end of the study period, which also happens to be a peak infection period while the exposure time associated with the booster group is skewed towards the back end, when infections are much lower.

For the Israel Booster study, the authors essentially confirmed the existence of such bias with the following sentences:

"During this time [ed: study period],the incidence of Covid-19 in Israel was one of the highest in the world."

"The incidence of Covid-19 and thus exposure to SARS-CoV-2 changed during the study period."

Given that at the start of the study period, Israel's infection rate was "one of the highest in the world" and that the incidence and exposure subsequently "changed," this change represents a decrease in incidence and exposure. (The data can be found here. One of the charts shows the 60 and over age group.)

Reflecting the current state of medical "science," the authors didn't make the above statements in order to explain a source of bias. Instead, they used the first statement to explain why their study could achieve statistical significance on mortality due to Covid, which is a rare outcome, and they cited the second statement in order to make the false claim: "we assume that after adjustment for all covariates, including socioeconomic status, these changes had a similar effect in the booster group and the non-booster group."

Their "assumption" I just showed to not hold.

***

This is another example of the "background infection rate" bias that we described in our bias paper (link). In that paper, we used an example of a Danish study which also started when the infection rate peaked and then by the end of the study period, the infection rate had dropped to almost zero.

If the booster were to be completely useless, the average case rate in the no booster group would be higher than the average case rate in the booster group because of differential exposure time against a decreasing background infection rate. This leads to a high vaccine effectiveness when the effectiveness is assumed to be zero!

Adjusting for "all covariates" does not cure this bias whatsoever.

***

What can be done about such bias?

For one thing, better data disclosure. All these studies should show the distribution of exposure time, by treatment vs control group, over the study period. On top of that, we can superimpose the background infection rate. Such an analysis discloses the source of bias.

Next, attempt to do the same analysis for a different time period, especially one in which the infection rate trends in the opposite direction. In practice, this may be hard to accomplish if the public health department decided to launch vaccines around an infection peak.

How hard can counting be?

Raphael Lataster has written a response to our JECP paper, which discusses several biases in Covid-19 vaccine observational studies that have not been properly accounted for in many notable studies.

He augmented our first example to show another source of bias in later studies.

In our example, we demonstrated how the "case counting window bias" could cause vaccine effectiveness estimates to be over optimistic. In typical clinical trials, one starts counting cases (events) from the day the treatment is finished, so in the case of two-shot Covid-19 vaccines, this should be the day after the second dose. However, none of the Covid-19 VE results you have read about include all these cases!

All studies have imposed a case-counting window that always starts X days after the second dose. X is most often 14 days but sometimes it's 7 days, sometimes it's 28 days, or whatever the researchers deemed appropriate, frequently after computing VE for different window sizes.

The problem is that in observational studies, for the unvaccinated group, there is no such thing as 14 days after second shot (because they did not get any shots, unlike those in the clinical trial who got placebo shots). In many studies, the case-counting window is applied asymmetrically to the vaccinated group (reducing the case count) but not to the unvaccinated group.

Lataster pointed out another problem that creeped in with later studies. Many prominent studies started to define the "fully vaccinated" group as those having two doses (within some allowable dose duration) and who did not get infected prior to 14 days after the second shot, and then label the complement of the fully vaccinated group as the "unvaccinated" group.

This creates a host of problems. For the sake of discussion, let's focus on one subset: the group of doubly vaccinated people who got infected during the first 14 days after taking the second shot. In our original example, these cases are taken out of the case count in the vaccinated group. Effectively, these cases disappeared from the analysis.

In Lataster's example, these cases did not disappear. They got shifted into the unvaccinated group because that group now included doubly-vaccinated people who got infected in the first 14 days.

***

The decision to apply a case-counting window is tragic. It lands researchers into a dead end. This is a point Peter and I made in our reply to Lataster's response (here, paywalled).

The key of understanding our argument is to pay attention to both numerators and denominators in the case infection rates, which underlie the VE formula. The numerators are the cases, and the denominators are the subjects from which cases accrue.

In typical clinical trials, the treatment populations are fixed in advance. In an intent-to-treat analysis, one must use the treatment groups as originally randomized. Even in a per-protocol analysis, we remove subjects who did not complete the treatment (at the risk of adulterating the randomization). This procedure is different from removing subjects who completed the treatment (2 doses), and then got infected (i.e. have the primary outcome) within X days of finishing the treatment.

However, if the analyst uses the per-protocol population, and also applies the case-counting window, then these subjects who got infected during the first 14 days disappear from the numerator (case count) but not the denominator. In effect, they have become "immortal". Further, in observational studies, for which we cannot apply the case-counting window to the unvaccinated group, the analyst has made some immortals in the vaccinated group but not the unvaccinated group!

In Lataster's example, not only are the cases moved to the "unvaccinated" group but also the subjects. The analyst has taken the doubly-vaccinated person who got infected during the first 14 days out of the vaccinated group and added this person to the unvaccinated group. The case count follows along. This procedure makes me very uncomfortable. What happened here is that the analyst altered the treatment group assignment after looking at the primary outcome (Covid-19 cases).

This is why I called this a dead-end. If you just move the case not the group assignment, then you insert an immortal bias. If you move both the case and group assignment, you're manipulating the group assignment based on observing the primary outcome of the analysis. And, as Peter and I explained in our response, we are not convinced by arguments for case-counting windows.

***

Another part of Lataster's comment concerns empirical evidence that showed negative VE. I'm unwilling to go as far as he does because those negative VE numbers are observed in subgroup analyses for selected studies. Much more work needs to happen before we can establish generality of those results.

 

Rat czarina claims numbers don't lie

One of the most astounding news of 2023 must be the creation of the position of the "rat czarina" by the New York City mayor. Just last week, a friend was asking if I have noticed any improvement since she began her reign. I could not think of a single thing she has done. Well, this New York Post article tells us her accomplishments (link). She said "numbers don't lie".

She apparently created a new rule that says garbage cannot be put out on the sidewalk before 8 pm. As a result, "rat complaints to 311" went down by 26 percent compared to last June.

I immediately have a few questions: first, what was the level of April and May rat complaints compared to last April and May? also, what was the level of June all complaints compared to last June? what is the year-on-year variability of these levels?

Assuming that the stated causal relationship holds, the question is why? Presumably, when the garbage arrives later, the rats show up later, fewer people are outside to witness them, and so fewer complain. Does that solve the rat problem? Or just the rat complaint problem?

***

The next new rule is going to be forcing buildings to put their bags of trash inside storage containers.

The NYC mayor explained the logic of this rule with this amusing quip: "rats love garbage bags." So I guess he thinks rats hate storage containers.

I'm not sure they understand the problem. The storage bags would have been fine if people aren't dumpster-diving. You put something out there on the streets, and someone will show up to tear open the bags looking for stuff - food, stuff that people throw out to make space, empty beer cans, etc. This won't change if the bags are put inside storage containers!

 

Uninsightful by design

I saw the following chart in an article about the ordering of author names in research papers. This is a topic of great interest to researchers looking to become famous. Memorably, the article was written by two European researchers with the same first and last names.

 

The article investigates conventions of sequencing authors in scientific papers with more than one authors. The two most popular conventions are: order by significance of contribution ("importance"), or order alphabetically by first letter of last name.

It appears that the following analysis was performed to make the above chart: take all papers with exactly two authors, group by first character of first author's last name, then compute the probability that the last names are listed in alphabetical order, given the first character of the first author's last name.

There is a natural downward slope to this line: if the first author has a last name starting A, the proportion of papers for which the second author has a last name starting B, C, D,... or Z should be close to 100%. If the first author's last name begins with Z, there will be an overwhelming chance that the second author's last name starts with a letter before Z, which means that the pair of names would not be alphabetical.

This chart caught my attention because it's one of those charts that may be uninsightful by design.

***

Why can't it be insightful?

Let's start by finding a statistical model for the observed data (whether the pair of names are alphabetical). The order convention (by importance or by alphabet) is unobservable.

Assume we have a pair of authors. For a specific research paper, the pair is either listed alphabetically or not. If the authors are listed non-alphabetically, then we are sure that the order convention is not alphabetical - which for the purpose of this analysis, we assume to be by importance. By contrast, if the observed order is alphabetical, then either order convention could have generated it -- names being listed alphabetically does not exclude the possibility that they were ordered by importance!

In the article, the authors draw the following conclusion from the chart:

Statistics [green line] exceeds this baseline [bold black line] the most, indicating that many authors intentionally ordered their surnames alphabetically. By contrast, psychology [blue line] appears to be the discipline where the list of authors is mostly ordered by the maount of work contributed (i.e., the percentages are close to the baseline probabilities).

They see the signal in the gap between the value of a particular discipline and the "baseline" probability. If the proportion of papers with alphabetical ordering is higher, then these authors conclude that that discipline is more likely to prefer alphabetical ordering.

Must it be so?

***

Let's take an extreme case as a thought experiment. Assume that no publication uses alphabetical ordering. All authors are listed by importance of their contributions.

If we create the above chart, computing the proportion of alphabetically ordered names given the first letter of the first author's surname, it would look exactly the same - except that the horizontal axis should be relabeled "First letter of the primary author's last name" (instead of "First letter of the first author").

However, the gap between these lines gives us zero information about the preference for alphabetical ordering because all names are listed by importance, and some just happen to also be alphabetical. In this experiment, the gap is purely driven by the (chance?) pairing of authors.

Either the research doesn't accomplish what the researchers think it did, or I'm missing the point. What do you think?

Is it worth it to flout parking rules?

Significance magazine (link) has a fun article about parking in front of fire hydrants in New York City. It's great data journalism.

The researchers conducted a "field experiment" in which they observed "six routes through Manhattan streets" on July 11, 2022 from 1-5 pm, during which they observed 138 violations. They then merged the hand-collected data with NYC's open data recording all tickets, matching license-plate numbers to learn that only 7 of those drivers have been served tickets.

Based on that, they deduced that most drivers who park in front of hydrants get away with the violation. They computed a detection rate of 5% (= 7/138). During that period of time, the traffic cops issued 423 tickets, and therefore, they deduced that the total violations to be 423/5% = 8,460. This number includes both the 423 tickets and a further 8,037 instances for which no tickets were issued.

They now model the cat-and-mouse game between the rule-bending drivers and the cops as an "exponential game". A timer is started each time some driver parks at a hydrant. The game is to see whether the cop shows up to flag the violation first, or the driver returns to pick up the car first. The model assumes that the time until the next check is exponentially distributed. An exponential distribution is where most values are small, but a few values can be very large. Such a distribution is fully described by its average value, which is estimated to be 6 hours. On average, a cop checks a given hydrant once every 6 hours. (That's the average interval, but each interval has a different value.)

They apply the same exponential model structure for the rule-bending drivers. In this case, the time until the driver returns to a given hydrant - i.e. the duration of violation -  is exponentially distributed, with a mean of 18 minutes (0.3 hours). Comparing the two exponential distributions, we can already see that drivers who leave their cars for a short period of time (say under 60 minutes) have a low chance of getting ticketed but if they park their cars illegally for hours at a time, their risk of detection is much higher. The authors did these calculations: the probability of detection is 16% for one hour, and increases to 99% for 24 hours.

Given the above model - and we assume also that the cops and the drivers act independently, the probability that the cop arrives before the driver returns is the key statistic we care about. That's the chance of the driver receiving a ticket, which as we know from above, is 5% based on the observed data. A consequence of the exponential game model is that this number is the average time until a cop arrives divided by the sum of the average times of a cop arriving and of the driver returning. Thus, 0.05 = 0.3/(0.3+6). [This verifies that the above calculation is correct.]

***

This type of model has been deployed to analyze gambling. If one buys lottery tickets every day, what is the chance that one hits the jackpot before one goes broke?

***

What's left unexplained is how they got the 6-hour estimate for the time until detection. This is a clever bit of work. Remember the researchers matched a subset of the observed violations to actual tickets issued. For these violations, the researchers determined the duration between observing the violation and issuing the ticket to be 6 hours on average.

But... that duration is counted from the moment the researchers found the illegally-parked car, not from the moment the driver parked illegally. What's unknown is the passage of time before the researchers documented the violation.

Conveniently, that unknown duration can be ignored. This convenience comes with using the exponential model. In the exponential world, the future does not depend on the past. Let's say the car has been illegally parked for 10 minutes already. How much time will elapse before a cop shows up? The answer is the same as before: it's exponentially distributed with average of 6 hours.

***

Based on the math above, the researchers found that illegally parking makes sense. The penalty for getting caught is $115. Returning within 5 minutes limits the expected penalty to under $2, which is similar to the cost of feeding a parking meter.

 

P.S. [7/10/2023] Corrected "flout" in the title of the post. Thanks to the reader who alerted me to this.