## Too Much Churn: Estimating Customer Churn

18 Nov

A new paper uses financial transaction data to estimate customer churn in consumer-facing companies. The paper defines churn as follows:

There are three concerns with the definition:

1. The definition doesn’t make clear what is the normalizing constant for calculating the share. Given that the value “can vary between zero and one,” presumably the normalizing constant is either a) total revenue in the same year in which customer buys products, b) total revenue in the year in which the firm revenue was greater.
2. If the denominator when calculating s_fit is the total revenue in the same year in which the customer buys products from the company, it can create a problem. Consider a case where there is a customer that spends $10 in both year t and year t-k. And assume that the firm’s revenue in the same years is$10 and $20 respectively. In this case, the customer hasn’t changed his/her behavior but their share has gone from 1 to .5. 3. Beyond this, there is a semantic point. Churn is generally used to refer to attrition. In this case, it covers both customer acquisition and attrition. It also covers both a reduction and an increase in customer spending. A Fun Aside “Netflix similarly was not in one of our focused consumer-facing industries according to our SIC classification (it is found with two-digit SIC of 78, which mostly contains movie producers)” — this tracks with my judgment of Netflix. ## 94.5% Certain That Covid Vaccine Will Be Less Than 94.5% Effective 16 Nov “On Sunday, an independent monitoring board broke the code to examine 95 infections that were recorded starting two weeks after volunteers’ second dose — and discovered all but five illnesses occurred in participants who got the placebo.” Moderna Says Its COVID-19 Vaccine Is 94.5% Effective In Early Tests The data = control group is 5 out of 15k and the treatment group is 90 out of 15k. The base rate (control group) is .6%. When the base rate is so low, it is generally hard to be confident about the ratio (1 – (5/95)). But noise is not the same as bias. One reason to think why 94.5% is an overestimate is simply because 94.5% is pretty close to the maximum point on the scale. The other reason to worry about 94.5% is that the efficacy of a Flu vaccine is dramatically lower. (There is a difference in the time horizons over which effectiveness is measured for Flu for Covid, with Covid being much shorter, but useful to take that as a caveat when trying to project the effectiveness of Covid vaccine.) ## Fat Or Not: Toward ‘Proper Training of DL Models’ 16 Nov A new paper introduces a DL model to enable ‘computer aided diagnosis of obesity.’ Some concerns: 1. Better baselines: BMI is easy to calculate and it would be useful to compare the results to BMI. 2. Incorrect statement: The authors write: “the data partition in all the image sets are balanced with 50 % normal classes and 50 % obese classes for proper training of the deep learning models.” (This ought not to affect the results reported in the paper.) 3. Ignoring Within Person Correlation: The paper uses data from 100 people (50 fat, 50 healthy) and takes 647 images of them (310 obese). It then uses data augmentation to expand the dataset to 2.7k images. But in doing the train/test split, there is no mention of splitting by people, which is the right thing to do. Start with the fact that you won’t see the people in your training data again when you put the model in production. If you don’t split train/test by people, it means that the images of the people in the training set are also in the test set. This means that the test set accuracy is likely higher than if you would run it on a fresh sample. ## Not So Robust: The Limitations of “Doubly Robust” ATE Estimators 16 Nov Doubly Robust (DR) estimators of ATE are all the rage. One popular DR estimator is Robins’ Augmented IPW (AIPW). The reason why Robins’ AIPW estimator is called doubly robust is that if either your IPW model or your y ~ x model is correctly specified, you get ATE. Great! Calling something “doubly robust” (DR) makes you think that the estimator is robust to (common) violations of commonly made assumptions. But DR replaces one strong assumption with one marginally less strong assumption. It is common to assume that IPW or Y ~ X are right. But DR replaces either of these with the OR clause. So how common is it to get either of the models right? Basically never. If neither model is right, you multiply the bias terms. And that ought to blow up the bias. (There is one more reason to worry about the use of word ‘robust.’ In statistics, it is used to convey robustness of to violations of distributional assumptions.) Given the small advance in assumptions, it turns out that the results aren’t better either (and can be substantially worse): 1. “None of the DR methods we tried … improved upon the performance of simple regression-based prediction of the missing values. (see here.) 2. “The methods with by far the worst performance with regard to RSMSE are the Doubly Robust (DR) approaches, whose RSMSE is two or three times as large as the RSMSE for the other estimators.” (see here and the relevant table is included below.) Some people prefer DR for efficiency. But the claim for efficiency is based on strong assumptions being met: “The local semiparametric efficiency property, which guarantees that the solution to (9) is the best estimator within its class, was derived under the assumption that both models are correct. This estimate is indeed highly efficient when the π-model is true and the y-model is highly predictive.” p.s. When I went through some of the lecture notes posted online, I was surprised that the lecture notes explain DR as “if A or B hold, we get ATE” but do not discuss the modal case. ## Instrumental Music: When It Rains, It Pours 23 Oct In a new paper, Jon Mellon reviews 185 papers that use weather as an instrument and finds that researchers have linked 137 variables to weather. You can read it as each paper needing to contend with 136 violations of the exclusion restriction, but the situation is likely less dire. For one, weather as an instrument has many varietals. Some papers use local (both in time and space) fluctuations in the weather for identification. At the other end, some use long-range (both in time and space) variations in weather, e.g., those wrought upon by climate. And the variables affected by each are very different. For instance, we don’t expect long-term ‘dietary diversity’ to be affected by short-term fluctuations in the local weather. A lot of the other variables are like that. For two, the weather’s potential pathways to the dependent variable of interest are often limited. For instance, as Jon notes, it is hard to imagine how rain on election day would affect government spending any other way except its effect on the election outcome. There are, however, some potential general mechanisms through which exclusion restriction could be violated. The first that Jon identifies is also among the oldest conjecture in social science research—weather’s effect on mood. Except that studies that purport to show the effect of weather on mood are themselves subject to selective response, e.g., when the weather is bad, more people are likely to be home, etc. There are some other more fundamental concerns with using weather as an instrument. First, when there are no clear answers on how an instrument should be (ahem!) instrumented, the first stage of IV is ripe for specification search. In such cases, people probably pick up the formulation that gives the largest F-stat. Weather falls firmly in this camp. For instance, there is a measurement issue about how to measure rain. Should it be the amount of rain or the duration of rain, or something else? And then there is a crudeness issue of the instrument as ideally, we would like to measure rain over every small geographic unit (of time and space). To create a summary measure from crude observations, we often need to make judgments, and it is plausible that judgments that lead to a larger F-stat. are seen as ‘better.’ Second, for instruments that are correlated in time, we need to often make judgments to regress out longer-term correlations. For instance, as Jon points out, studies that estimate the effect of rain on voting on election day may control long-term weather but not ‘medium term.’ “However, even short-term studies will be vulnerable to other mechanisms acting at time periods not controlled for. For instance, many turnout IV studies control for the average weather on that day of the year over the previous decade. However, this does not account for the fact that the weather on election day will be correlated with the weather over the past week or month in that area. This means that medium-term weather effects will still potentially confound short-term studies.” The concern is wider and includes some of the RD designs that measure the effect of ad exposure on voting, etc. ## Distance Function For Matched Randomization 6 Oct What is the right distance function for creating greater balance before we randomize? One way to do it is not to think too much about the distance function at all. For instance, this paper takes all the variables, treats them as the same (you can do normalization if you want to) and you can use Mahalanobis distance, or what have you. There are two decisions here: about the subspace and about the weights. Surprisingly, these ad hoc choices don’t have serious pitfalls except that the balance we get finally in the Y_0 (which is the quantity of interest) may not be great. There is also one case where the method will fail. The point is best illustrated with a contrived example. Imagine there is just one observed X and let’s say it is pure noise. If we were to match on noise and then randomize, it will be the case that it will increase the imbalance in the Y_0 half the time and decrease it another half the time. In all, the benefit of spending a lot of energy on improving balance in an ad hoc space, which may or may not help the true objective function, is likely overstated. If we have a baseline survey and baseline Ys and we assume that Y_lagged predicts Y_0, then the optimal strategy would be to match on lagged Y. If we have multiple time periods for which we have surveys, we can build a supervised learning model to predict Y in the next time period and match on the Y_hat. The same logic applies when we don’t have lagged_Y for all the rows. We can impute them with supervised learning. ## Unmatched: The Problem With Comparing Matching Methods 5 Oct In many matching papers, the key claim proceeds as follows: our matching method is better than others because on this set of contrived data, treatment effect estimates are closest to those from the ‘gold standard’ (experimental evidence). Let’s side-step concerns related to an important point: evidence that a method works better than other methods on some data is hard to interpret as we do not know if the fact generalizes. Ideally, we want to understand the circumstances in which the method works better than other methods. If the claim is that the method always works better, then prove it. There is a more fundamental concern here. Matching changes the estimand by pruning some of the data as it takes out regions with low support. But the regions that are taken out vary by the matching method. So, technically the estimands that rely on different matching methods are different—treatment effect over different sets of rows. And if the estimate from method X comes closer to the gold standard than the estimate from method Y, it may be because the set of rows method X selects produce a treatment effect that is closer to the gold standard. It doesn’t however mean that method X’s inference on the set of rows it selects is the best. (And we do not know how the estimate technically relates to the ATE.) ## Optimal Recruitment For Experiments: Using Pair-Wise Matching Distance to Guide Recruitment 4 Oct Pairwise matching before randomization reduces s.e. (see here, for instance). Generally, the strategy is used to create balanced control and treatment groups from available observations. But we can use the insight for optimal sample recruitment especially in cases where we have a large panel of respondents with baseline data, like YouGov. The algorithm is similar to what YouGov already uses, except it is tailored to experiments: 1. Start with a random sample. 2. Come up with optimal pairs based on whatever criteria you have chosen. 3. Reverse sort pairs by distance with the pairs with the largest distance at the top. 4. Find the best match in the rest of the panel file for one of the randomly chosen points in the pair. (If you have multiple equivalent matches, pick one at random.) 5. Proceed as far down the list as needed. Technically, we can go from step 1 to step 4 if we choose a random sample that is half the size we want for the experiment. We just need to find the best matching pair for each respondent. ## Another ANES Goof-em-up: VCF0731 30 Aug At this point, it’s well established that the ANES CDF’s codebook is not to be trusted (I’m repeating “not to be trusted to include a second link!). Recently, I stumbled across another example of incorrect coding in the cumulative data file, this time in VCF0731 – Do you ever discuss politics with your family or friends? The codebook reports 5 levels: Do you ever discuss politics with your family or friends? 1. Yes 5. No 8. DK 9. NA INAP. question not used However, when we load the variable and examine the unique values: # pulling anes-cdf from a GitHub repository cdf <- rio::import("https://github.com/RobLytle/intra-party-affect/raw/master/data/raw/cdf-raw-trim.rds") unique(cdf$VCF0731)
## [1] NA  5  1  6  7

We see a completely different coding scheme. We are left adrift, wondering “What is 6? What is 7?” Do 1 and 5 really mean “yes” and “no”?

We may never know.

For a survey that costs several million dollars to conduct, you’d think we could expect a double-checked codebook (or at least some kind of version control to easily fix these things as they’re identified).

## AFib: Apple Watch Did Not Increase Atrial Fibrillation Diagnoses

28 Aug

A new paper purportedly shows that the release of Apple Watch 2018 which supported ECG app did not cause an increase in AFib diagnoses (mean = −0.008).

They make the claim based on 60M visits from and 1270 practices across 2 years.

Here are some things to think about:

1. Expected effect size. Say the base AF rate as .41%. Let’s say 10% has the ECG app + Apple watch. (You have to make some assumptions about how quickly people downloaded the app. I am making a generous assumption that 10% do it the day of release.) For the 10%, say it is .51%. Add’l diagnoses expected = .01*30M ~ 3k.
2. Time trend. 2018-19 line is significantly higher (given the baseline) than 2016-2017. It is unlikely to be explained by the aging of the population. Is there a time trend? What explains it? More acutely, diff. in diff. doesn’t account for that.
3. Choice of the time period. When you have observations over multiple time periods pre-treatment and post-treatment, the inference depends on which time period you use. For instance,  if I do an “ocular distortion test”, the diff. in diff. with observations from Aug./Sep. would suggest a large positive impact. For a more transparent account of assumptions, see diff.healthpolicydatascience.org (h/t Kyle Foreman).
4. Clustering of s.e. Some correlation in diagnosis because of facility (doctor) which is unaccounted for.

## Survey Experiments With Truth: Learning From Survey Experiments

27 Aug

Tools define science. Not only do they determine how science is practiced but also what questions are asked. Take survey experiments, for example. Since the advent of online survey platforms, which made conducting survey experiments trivial, the lure of convenience and internal validity has persuaded legions of researchers to use survey experiments to understand the world.

Conventional survey experiments are modest tools. Paul Sniderman writes,

“These three limitations of survey experiments—modesty of treatment, modesty of scale, and modesty of measurement—need constantly to be borne in mind when brandishing term experiment as a prestige enhancer.” I think we can easily collapse these in two — treatment (which includes ‘scale’ as he defines it— the amount of time) and measurement.

Paul Sniderman

Note: We can collapse these three concerns into two— treatment (which includes ‘scale’ as Paul defines it— the amount of time) and measurement.

But skillful artisans have used this modest tool to great effect. Famously, Kahneman and Tversky used survey experiments, e.g., Asian Disease Problem, to shed light on how people decide. More recently, Paul Sniderman and Tom Piazza have used survey experiments to shed light on an unsavory aspect of human decision making: discrimination. Aside from shedding light on human decision making, researchers have also used survey experiments to understand what survey measures mean, e.g., Ahler and Sood

The good, however, has come with the bad; insight has often come with irreflection. In particular, Paul Sniderman implicitly points to two common mistakes that people make:

1. Not Learning From the Control Group. The focus on differences in means means that we sometimes fail to reflect on what the data in the Control Group tells us about the world. Take the paper on partisan expressive responding, for instance. The topline from the paper is that expressive responding explains half of the partisan gap. But it misses the bigger story—the partisan differences in the Control Group are much smaller than what people expect, just about 6.5% (see here). (Here’s what I wrote in 2016.)
2. Not Putting the Effect Size in Context. A focus on significance testing means that we sometimes fail to reflect on the modesty of effect sizes. For instance, providing people $1 for a correct answer within the context of an online survey interview is a large premium. And if providing a dollar each on 12 (included) questions nudges people from an average of 4.5 correct responses to 5, it suggests that people are resistant to learning or impressively confident that what they know is right. Leaving$7 on the table tells us more than the .5, around which the paper is written.

More broadly, researchers are obtuse to the point that sometimes what the results show is how impressively modest the movement is when you ratchet up the dosage. For instance, if an overwhelming number of African Americans favor Whites who have scored just a few points more than a Black student, it is a telling testament to their endorsement of meritocracy.

## Nothing to See Here: Statistical Power and “Oversight”

13 Aug

“Thus, when we calculate the net degree of expressive responding by subtracting the acceptance effect from the rejection effect—essentially differencing off the baseline effect of the incentive from the reduction in rumor acceptance with payment—we find that the net expressive effect is negative 0.5%—the opposite sign of what we would expect if there was expressive responding. However, the substantive size of the estimate of the expressive effect is trivial. Moreover, the standard error on this estimate is 10.6, meaning the estimate of expressive responding is essentially zero.

https://journals.uchicago.edu/doi/abs/10.1086/694258

(Note: This is not a full review of all the claims in the paper. There is more data in the paper than in the quote above. I am merely using the quote to clarify a couple of statistical points.)

There are two main points:

1. The fact that estimate is close to zero and the s.e. is super fat are technically unrelated. The last line of the quote, however, seems to draw a relationship between the two.
2. The estimated effect sizes of expressive responding in the literature are much smaller than the s.e. Bullock et al. (Table 2) estimate the effect of expressive responding at about 4% and Prior et al. (Figure 1) at about ~ 5.5% (“Figure 1(a) shows, the model recovers the raw means from Table 1, indicating a drop in bias from 11.8 to 6.3.”). Thus, one reasonable inference is that the study is underpowered to reasonably detect expected effect sizes.

## Casual Inference: Errors in Everyday Causal Inference

12 Aug

Why are things the way they are? What is the effect of something? Both of these reverse and forward causation questions are vital.

When I was at Stanford, I took a class with a pugnacious psychometrician, David Rogosa. David had two pet peeves, one of which was people making causal claims with observational data. And it is in David’s class that I learned the pejorative for such claims. With great relish, David referred to such claims as ‘casual inference.’ (Since then, I have come up with another pejorative phrase for such claims—cosal inference—as in merely dressing up as causal inference.)

It turns out that despite its limitations, casual inference is quite common. Here are some fashionable costumes:

1. 7 Habits of Successful People: We have all seen business books with such titles. The underlying message of these books is: adopt these habits, and you will be successful too! Let’s follow the reasoning and see where it falls apart. One stereotype about successful people is that they wake up early. And the implication is you wake up early you can be successful too. It *seems* right. It agrees with folk wisdom that discomfort causes success. But can we reliably draw inferences about what less successful people should do based on what successful people do? No. For one, we know nothing about the habits of less successful people. It could be that less successful people wake up *earlier* than the more successful people. Certainly, growing up in India, I recall daily laborers waking up much earlier than people living in bungalows. And when you think of it, the claim that servants wake up before masters seems uncontroversial. It may even be routine enough to be canonized as a law—the Downtown Abbey law. The upshot is that when you select on the dependent variable, i.e., only look at cases where the variable takes certain values, e.g., only look at the habits of financially successful people, even correlation is not guaranteed. This means that you don’t even get to mock the claim with the jibe that “correlation is not causation.”

Let’s go back to Goji’s delivery service for another example. One of the ‘tricks’ that we had discussed was to sample failures. If you do that, you are selecting on the dependent variable. And while it is a good heuristic, it can lead you astray. For instance, let’s say that most of the late deliveries our early morning deliveries. You may infer that delivering at another time may improve outcomes. Except, when you look at the data, you find that the bulk of your deliveries are in the morning. And the rate at which deliveries run late is *lower* early morning than during other times.

There is a yet more famous example of things going awry when you select on the dependent variable. During World War II, statisticians were asked where the armor should be added on the planes. Of the aircraft that returned, the damage was concentrated in a few areas, like the wings. The top-of-head answer is to suggest we reinforce areas hit most often. But if you think about the planes that didn’t return, you get to the right answer, which is that we need to reinforce areas that weren’t hit. In literature, people call this kind of error, survivorship bias. But it is a problem of selecting on the dependent variable (whether or not a plane returned) and selecting on planes that returned.

2. More frequent system crashes cause people to renew their software license. It is a mistake to treat correlation as causation. There are many different reasons behind why doing so can lead you astray. The rarest reason is that lots of odd things are correlated in the world because of luck alone. The point is hilariously illustrated by a set of graphs showing a large correlation between conceptually unrelated things, e.g., there is a large correlation between total worldwide non-commercial space launches and the number of sociology doctorates that are awarded each year.

A more common scenario is illustrated by the example in the title of this point. Commonly, there is a ‘lurking’ or ‘confounding’ variable that explains both sides. In our case, the more frequently a person uses a system, the more the number of crashes. And it makes sense that people who use the system most frequently also need the software the most and renew the license most often.

Another common but more subtle reason is called Simpson’s paradox. Sometimes the correlation you see is “wrong.” You may see a correlation in the aggregate, but the correlation runs the opposite way when you break it down by group. Gender bias in U.C. Berkeley admissions provides a famous example. In 1973, 44% of the men who applied to graduate programs were admitted, whereas only 35% of the women were. But when you split by department, which eventually controlled admissions, women generally had a higher batting average than men. The reason for the reversal was women applied more often to more competitive departments, like—-wait for it—-English and men were more likely to apply to less competitive departments like Engineering. None of this is to say that there isn’t bias against women. It is merely to point out that the pattern in aggregated data may not hold when you split the data into relevant chunks.

It is also important to keep in mind the opposite of correlation is not causation—lack of correlation does not imply a lack of causation.

3. Mayor Giuliani brought the NYC crime rate down. There are two potential errors here:
• Forgetting about ecological trends. Crime rates in other big US cities went down at the same time as they did in NY, sometimes more steeply. When faced with a causal claim, it is good to check how ‘similar’ people fared. The Difference-in-Differences estimator that builds on this intuition.

4. I took this homeopathic medication and my headache went away. If the ailments are real, placebo effects are a bit mysterious. And mysterious they may be but they are real enough. Not accounting for placebo effects misleads us to ascribe the total effect to the medicine.

5. Shallow causation. We ascribe too much weight to immediate causes than to causes that are a few layers deeper.

6.  Monocausation: In everyday conversations, it is common for people to speak as if x is the only cause of y.

7.  Big Causation: Another common pitfall is reading x causes y as x causes y to change a lot. This is partly a consequence of mistaking statistical significance with substantive significance, and partly a consequence of us not paying close enough attention to numbers.

8. Same Effect: Lastly, many people take causal claims to mean that the effect is the same across people.

## Reliable Respondents

23 Jul

Setting aside concerns about sampling, the quality of survey responses on popular survey platforms is abysmal (see here and here). Both insincere and inattentive respondents are at issue. A common strategy for identifying inattentive respondents is to use attention checks. However, many of these attention checks stick out like sore thumbs. The upshot is that an experience respondent can easily spot them. A parallel worry about attention checks is that inexperienced respondents may be confused by them. To address the concerns, we need a new way to identify inattentive respondents. One way to identify such respondents is to measure twice. More precisely, measure immutable or slowly changing traits, e.g., sex, education, etc., twice across closely spaced survey waves. Then, code cases where people switch answers across the waves on such traits as problematic. And then, use survey items, e.g., self-reports and metadata, e.g., survey response time, metadata on IP addresses, etc. in the first survey to predict problematic switches using modern ML techniques that allow variable selection like LASSO (space is at a premium). Assuming the equation holds, future survey creators can use the variables identified by LASSO to identify likely inattentive respondents.

## Self-Recommending: The Origins of Personalization

6 Jul

Recommendation systems are ubiquitous. They determine what videos and news you see, what books and products are ‘suggested’ to you, and much more. If asked about the origins of personalization, my hunch is that some of us will pin it to the advent of the Netflix Prize. Wikipedia goes further back—it puts the first use of the term ‘recommender system’ in 1990. But the history of personalization is much older. It is at least as old as heterogeneous treatment effects (though latent variable models might be a yet more apt starting point). I don’t know for how long we have known about heterogeneous treatment effects but it can be no later than 1957 (Cronbach and Goldine Gleser, 1957).

Here’s Ed Haertel:

This episode reminded me of the “longstanding principle in statistics, which is that, whatever you do, somebody in psychometrics already did it long before. I’ve noticed this a few times.”

Reading Cronbach today is also sobering in a way. It shows how ad hoc the investigation of theories and coming up with the right policy interventions was.

## Interacting With Human Decisions

29 Jun

In sport, as in life, luck plays a role. For instance, in cricket, there is a toss at the start of the game. And the team that wins the toss wins the game 3% more often. The estimate of the advantage from winning the toss, however, is likely an underestimate of the maximum potential benefit of winning the toss. The team that wins the toss gets to decide whether to bat or bowl first. And 3% reflects the maximum benefit only when the team that won the toss chooses optimally.

The same point applies to estimates of heterogeneity. Say that you estimate how the probability of winning varies by the decision to bowl or bat first after winning the toss. (The decision to bowl or bat first is made before the toss.) And say, 75% of the time team that wins the toss chooses to bat first and wins these games 55% of the time. 25% of the time, teams decide to bowl first and win about 47% of these games. Winning rates of 55% and 47% would be likely yet higher if the teams chose optimally.

In the absence of other data, heterogeneous treatment effects give clear guidance on where the payoffs are higher. For instance, if you find that showing an ad on Chrome has a larger treatment effect, barring other information (and concerns), you may want to only show ads to people who use Chrome to increase the treatment effect. But the decision to bowl or bat first is not a traditional “covariate.” It is a dummy that captures the human judgment about pre-match observables. The interpretation of the interaction term thus needs care. For instance, in the example above, the winning percentage of 47% for teams that decide to bowl first looks ‘wrong’—how can the team that wins the toss lose more often than win in some cases? Easy. It can happen because the team decides to bowl in cases where the probability of winning is lower than 47%. Or it can be that the team is making a bad decision when opting to bowl first.

## Lost Years: From Lost Lives to Life Lost

2 Apr

The mortality rate is puzzling to mortals. A better number is the expected number of years lost. (A yet better number would be quality-adjusted years lost.) To make it easier to calculate the expected years lost, Suriyan and I developed a Python package that uses the SSA actuarial data and life table to estimate the expected years lost.

We illustrate the use of the package by estimating the average number of years by which people’s lives are shortened due to coronavirus (see Note 1 at the end of the article). Using data from Table 1 of the paper that gives us the distribution of ages of people who died from COVID-19 in China, with conservative assumptions (assuming the gender of the dead person to be male, taking the middle of age ranges) we find that people’s lives are shortened by about 11 years on average. These estimates are conservative for one additional reason: there is likely an inverse correlation between people who die and their expected longevity. And note that given a bulk of the deaths are among older people, when people are more infirm, the quality-adjusted years lost is likely yet more modest. Given that the last life tables from China are from 1981 and given life expectancy in China has risen substantially since then (though most gains come from reductions in childhood mortality, etc.), we exploit the recent data from the US, assuming as-if people have the same life tables as Americans. Using the most recent SSA data, we find that the number to be 16. Compare this to deaths from road accidents, the modal reason for death among 5-24, and 25-44 ages in the US. Assuming everyone who dies from a traffic accident is a man, and assuming the age of death to be 25, we get ~52 years, roughly 3x as large as that of coronavirus (see Note 3 at the end of the article). On the other hand, smoking on average shortens life by about seven years. (See Note 2 at the end of the article.)

8/4 Addendum: Using COVID-19 Electronic Death Certification Data (CEPIDC), like above, we estimate the average number of years lost by people dying of coronavirus. With conservative assumptions (assuming the gender of the dead person to be male, taking the middle of age ranges) we find that people’s lives are shortened by about 9 years on average. Surprisingly, the average number of years lost of the people dying of coronavirus remained steady at about 9 years between March and July 2020.

Note 1: Years lost is not sufficient to understand the impact of Covid-19. Covid-19 has had dramatic consequences on the quality of life and has had a large financial impact, among other things. It is useful to account for those when estimating the net impact of Covid-19.

Note 2: In the calculations above, we assume that all the deaths from Coronavirus have been observed. One could do the calculation differently by tracking life spans of people infected with Covid-19 and comparing it to a similar set of people who were never infected with Covid-19. Presumably, the average years lost for people who don’t die of Covid-19 when they are first infected is a lot lower. Thus, counting them would bring the average years lost way down.

Note 3: The net impact of Covid-19 on years lost in the short-term should plausibly account for years saved because of fewer traffic accidents, etc.

## Feigning Competence: Checklists For Data Science

25 Jan

You may have heard that most published research is false (Ionnadis). But what you probably don’t know is that most corporate data science is also false.

Gaurav Sood

The returns on data science in most companies are likely sharply negative. There are a few reasons for that. First, as with any new ‘hot’ field, the skill level of the average worker is low. Second, the skill level of the people managing these workers is also low—most struggle to pose good questions, and when they stumble on one, they struggle to answer it well. Third, data science often fails silently (or there is enough corporate noise around it that most failures are well-hidden in plain sight), so the opportunity to learn from mistakes is small. And if that was not enough, many companies reward speed over correctness, and in doing that, often obtain neither.

How can we improve on the status quo? The obvious remedy for the first two issues is to increase the skill by improving training or creating specializations. And one remedy for the latter two points is to create incentives for doing things correctly.

Increasing training and creating specializations in data science is expensive and slow. Vital, but slow. Creating the right incentives for good data science work is not trivial either. There are at least two large forces lined up against it: incompetent supervisors and the fluid and collaborative nature of work—work usually involves multiple people, and there is a fluid exchange of ideas. Only the first is fixable—the latter is a property of work. And fixing it comes down to making technical competence a much more important criterion for hiring.

Aside from hiring more competent workers or increasing the competence of workers, you can also simulate the effect by using checklists—increase quality by creating a few “pause points”—times during a process where the person (team) pauses and goes through a standard list of questions.

To give body to the boast, let me list some common sources of failures in DS and how checklists at different pause points may reduce failure.

1. Learn what you will lose in translation. Good data science begins with a good understanding of the problem you are trying to solve. Once you understand the problem, you need to translate it into a suitable statistical analog. During translation, you need to be aware that you will lose something in the translation.
2. Learn the limitations. Learn what data you would love to have to answer the question if money was no object. And use it to understand how far do you fall short from that ideal and then come to a judgment about whether the question can be answered reasonably with the data at hand.
3. Learn how good the data are. You may think you have the data, but it is best to verify it. For instance, it is good practice to think through the extent to which a variable captures the quantity of interest.
4. Learn the assumptions behind the formulas you use and test the assumptions to find the right thing to do. Thou shall only use math formulas when you know the limitations of such formulas. Having a good grasp of when formulas don’t work is essential. For instance, say the task is to describe a distribution. Someone may use the mean and standard deviation to describe it. But we know that these sufficient statistics vary by distribution. For binomial, it may just be p. A checklist for “describing” a variable can be:
1. check skew by plotting: averages are useful when distributions are symmetric, and lots of observations are close to the mean. If skewed, you may want to describe various percentiles.
2. how many missing values and what explains the missing values.
3. check for unusual values and what explains the ‘unusual’ values.

## Ruling Out Explanations

22 Dec

The paper (pdf) makes the case that the primary reason for electoral cycles in dissents is priming. The paper notes three competing explanations: 1) caseload composition, 2) panel composition, and 3) volume of caseloads. And it “rules them out” by regressing case type, panel composition, and caseload on quarters from the election (see Appendix Table D). The coefficients are uniformly small and insignificant. But is that enough to rule out alternate explanations? No. Small coefficients don’t imply that there is no path from proximity to the election via competing mediators to dissent (if you were to use causal language). We can only conclude that the pathway doesn’t exist if there is a sharp null. The best you can do is bound the estimated effect.

## Learning From the Future with Fixed Effects

6 Nov

Say that you want to predict wait times at restaurants using data with four columns: wait times (wait), the restaurant name (restaurant), time and date of observation. Using the time and date of the observation, you create two additional columns: time of the day (tod) and day of the week (dow). And say that you estimate the following model:

$\text{wait} \sim \text{restaurant} + tod + dow + \epsilon$

Assume that the number of rows is about 100 times the number of columns. There is little chance of overfitting. But you still do an 80/20 train/test split and pick the model that works the best OOS.

You have every right to expect the model’s performance to be close to its OOS performance. But when you deploy the model, the model performs much worse than that. What could be going on?

In the model, we estimate a restaurant level intercept. But in estimating the intercept, we use data from all wait times, including those that happened after the date. One fix is to using rolling averages or last X wait times in the regression. Another is to more formally construct the data in such a way that you are always predicting the next wait time.