The Verification Venue · a fear pointed at the wrong vehicle

The Trip That Flips the Fear

You grip the armrest at takeoff and let your guard down behind the wheel. For the same point-to-point trip, that is exactly backwards: the drive is the part that should scare you, not the flight.

A micromort is a clean way to hold danger in your hand: one micromort is a one-in-a-million chance of sudden death (Ronald Howard, 1980; popularised by David Spiegelhalter). It turns "is flying safer than driving?" into arithmetic. Type in a trip below and watch the micromorts pile up for each way of making it — every number recomputed, live, from the raw 2023 death counts, not a quoted slogan.

The bars don't lie because the rates underneath them are taken from public counts, not vibes. The flight's risk is so much smaller that it nearly vanishes — and that's the point: cruising at 35,000 feet is one of the safest things a human can do per mile. The danger you feel is real danger, just attached to the wrong half of the journey.

But "per mile" is only one ruler

Every bar above measures danger per mile. That already sounds neutral — and it hides a decision. A mile of flying and a mile of walking are the same distance but wildly different amounts of your life: the plane covers its mile in seven seconds, the walk in twenty minutes. Ask the same death counts a different question — per hour of travel, or per whole trip — and the safest mode is not the one you'd expect. Add every mode and switch the ruler. Watch the order rearrange.

The reorder is the whole point. Per mile, flying is untouchable — safer even than a bus, because a plane earns its safety by covering enormous distance. But that same speed is why the crown doesn't survive the switch to time: an hour aloft carries you five hundred miles, and it spends the plane's tiny per-mile risk over every one of them. Measured by the hour you actually sit there exposed, the humble bus wins, the train is next, and flying is merely ordinary — about as safe as the drive to the airport, not a hundred times safer. Nothing about the danger changed. Only the ruler did.

Whose average is it?

Everything above rests on one number for the road: 1.26 deaths per 100 million vehicle-miles. That is an average, and an average is a mixture. Poured into it: the motorcycle and the minivan, the county road at 3 a.m. and the Tuesday commute, the drunk driver and the sober one. Almost nobody is the average. So take the mixture apart, and find out whether the fear survives being aimed properly.

Conditioning a rate is one line of arithmetic, and the line repays staring at:

That single line is the whole instrument, and it is lopsided in a way that risk writing almost never admits. The top is always knowable. The Fatality Analysis Reporting System records every death on a public U.S. road, along with the road class, the light, the vehicle body, the restraint, the measured blood alcohol. Splitting deaths is a matter of counting, and this page counts them, from the raw case files rather than from anyone's summary table. The bottom is usually not knowable. Somebody has to have measured how many miles were driven under that condition, and for most conditions nobody has.

So every row below wears a badge for its denominator, and the badge is the honest part: counted a national traffic-counting programme publishes the miles; surveyed only a household travel survey estimates them; none nobody produces a figure at all. Pick a row and the panel underneath opens it up.

The top of that table is the footnote made good. A motorcycle carries well under one percent of America's traffic and more than fifteen percent of its traffic deaths, which puts a rider more than twenty times above the average per mile. That is the order of magnitude, and it is a measurement: both halves of the fraction are published, by two agencies that were not trying to make this point. Inside the road network alone the spread is about four and a half to one, from an urban freeway at the safe end to a rural major collector at the other, which is a fair description of the difference between a highway engineer's road and a road that was a farm track once.

Now look at the bottom three rows, and at the column that will not fill in. Those are not obscure conditions. They are, almost exactly, the argument everyone makes for why the average does not apply to them: I do not drink and drive. I wear my belt. I do not drive at night. Every one of those is a claim about a rate. Not one of them has a denominator. You can count the deaths to the last person, and the miles are simply not there, so the relative risk becomes whatever you decide it is. Drag the slider and watch a widely repeated safety fact swing by more than a factor of ten without a single new observation.

This is worth being careful about in both directions. The missing denominator does not mean the claim is false. Impaired driving really is enormously more dangerous per mile, unbelted occupants really do die at a rate their numbers cannot justify, and no one should read this page as a licence for either. What is missing is the size: impaired driving multiplies your risk per mile by somewhere between about six and about a hundred and fifty, and on the evidence assembled above, the slider is the only thing choosing.

The estimator that needs no denominator

Put the missing miles to one side and ask a narrower question. Not how much more dangerous is the unbelted population per mile, but what does the belt do. Two people are in one car when it leaves the road. One is wearing a belt and one is not. Nobody needs to know how far either of them drove that year to say which of them the tree treated worse.

That is double pair comparison, published by Leonard Evans in 1986 and NHTSA's standard belt method ever since. Take every vehicle in FARS carrying a subject and an other, where at least one of the two died. Inside a single crash the other occupant's deaths are a measure of how bad these crashes were: the speed, the angle, the tree, the vehicle, the road, and the disposition of whoever was driving. Form the ratio of subject deaths to other deaths separately for subjects who buckled and subjects who did not, then divide one ratio by the other. Everything the two people shared cancels, because they shared it. NHTSA's own statement of why this is worth doing: double pair comparison “implicitly ‘adjusts’ or ‘controls’ for the differences in the severity of crashes involving belted and unrestrained occupants.” No exposure data of any kind enters it. There is nothing to be missing.

Before it is pointed at anything, the estimator is checked against a case whose answer is already in print. NHTSA's 2017 evaluation works one all the way through on the page: four cells of centre-rear passengers and drivers, two separate estimates of 64.9% and 65.4%, and a combined 65.3%. Our implementation is handed those four cells first and has to return those three numbers, including NHTSA's own rounding of the intermediate ratios, or it exits without writing anything. It returns them.

Read the spread before you read the answer. The four cells give two separate estimates, one using the unbelted control and one using the belted control, and they are measuring the same thing by different routes. NHTSA states the test they constitute: “effectiveness should be the same relative to any valid control group used for the comparisons – if it varies substantially, then at least one of those comparison groups is not a valid control group.” In the front seats the two routes land about two to six points apart, which is agreement. In the back seats they land twelve and twenty points apart, which is the estimator telling you it is running out of data and that you should not trust the third decimal of anything below it. That alarm is printed above whether it is quiet or loud.

And the method's own lie detector. Belt use in FARS is what somebody wrote down, not what anybody saw, and after the belt laws arrived survivors began reporting belts they had not worn. NHTSA measured the size of that: the same vehicles gave a 47.81% fatality reduction in 1977 to 1985 data and an apparent 61.89% in 1986 to 1999 data, so they defined a universal exaggeration factor, (100 − 47.81) / (100 − 61.89) = 1.369, and deflate every front-seat estimate by it. We do the same, and print both numbers, because which one you are looking at is the entire difference between 61% and 47%. NHTSA does not deflate rear-seat estimates, on the evidence that rear passengers under- report rather than over-report belt use, and neither do we.

Does it work? The point of running it here was never to improve on NHTSA. It was to find out whether a stranger with a laptop and no exposure data can get their number, because a method that only works inside the agency that owns the files is not a method a reader can check. Four of the six pairings land on the published figure, including the canonical one: for front-seat car occupants NHTSA has published 45% since 1984, and seven years of recent data run through this script gives 47.3%. Two pairings miss, both of them light trucks and vans, where our estimate runs high. We can name the likely reason and cannot close it: NHTSA restricts its analyses to vehicles it can VIN-decode and confirm were equipped with the belt in question, and we take the body-type code at face value. That is a real gap and it is printed in the panel above rather than left out of the count.

Two questions wearing one sentence

So the column fills in, but it does not fill in the row that was empty. It is worth being exact about what just happened, because the two quantities get spoken as though they were one:

Double pair comparison answers the first. It says an unbelted car driver is about 1.9 times as likely to die as a belted one in the same crash. It cannot answer the second, because the second folds in how often each group crashes at all, and that is where the miles were needed. And the two are not close, because the people who do not buckle are not a random sample of drivers who happen to have skipped a step. From the same seven years of case files, drivers in fatal crashes whose belt state was recorded:

The first row of that table is an effect of not buckling and belongs to the belt. The night row and the age row are things that were true of the driver before the crash, and belong to the second question, not the first. The alcohol rows are the honest mess: an unbelted driver in a fatal crash is nearly twice as likely to have been tested for alcohol at all, and the reason is that they are far more likely to be dead, and the dead get tested. So the last row compares two groups selected differently and cannot be read as a clean prevalence. It is here because leaving it out would be worse: it is the row a reader would most want, and it is the row the data is least able to give.

That gap, between about 1.9 and the slider's ten-fold swing, is not error. It is the difference between a belt and a person who wears one, and no amount of case-file arithmetic can turn one into the other.

The denominator somebody went and measured

The other row without a denominator was alcohol, and there the fix is less clever and more laborious: if nobody counts the miles, go and sample the traffic. NHTSA's Virginia Beach crash risk study ran for twenty months, twenty-four hours a day, seven days a week. Crash-involved drivers were recruited at the scene. Then, for each one, two control drivers were taken “from traffic passing the crash location, driving in the same direction of travel, on the same day of week and at the same time of day one week later.”

That control sample is the missing denominator, and it was measured. It is not measured in miles. It is measured in drivers who were on that road at that hour, which for this question is the better unit anyway, because it holds the road, the hour and the day of week fixed instead of averaging over them. It also quietly answers the third condition on the list: the controls were drawn at the same time of night as the crashes, so the whole risk curve is already conditioned on when you drive.

The result, from 3,353 crash drivers and 6,868 control drivers who gave breath samples: adjusted for age and gender, a driver at 0.05 is about 2 times as likely to crash as a driver at zero, at 0.08 about 4 times, at 0.10 about 5.5 times, at 0.15 about 12 times, and at 0.20 and above more than 23 times. Those are numbers with a denominator behind them.

One check worth doing by hand, because it shows what a bucket costs. The study's raw counts put 95 of 3,353 crash drivers above 0.08 against 26 of 6,868 controls, which is an odds ratio of (95/3258) / (26/6842) = 7.7. That is nearly twice the modelled figure at 0.08, and the difference is not a contradiction: above 0.08 is a bucket running up past 0.20, where the risk is more than twenty-fold, while at 0.08 is a single point on a curve that is still climbing steeply. A range and a point are different claims, and a great deal of alcohol statistics is the two being quoted as one.

What this section did not close. Driving at night, taken on its own and separately from alcohol, still has no per-mile denominator here. The case-control design absorbs the hour rather than measuring it, which is exactly what makes the alcohol curve trustworthy and exactly why it cannot be turned round to price the night. The honest state of the three rows is now: the belt is measured by a design that needs no exposure, alcohol is measured against a sampled exposure, and the night is still a slider.

Can you drive your way to airline safety?

This is the question the conditioning was really for. If the average driver is roughly a hundred times worse per mile than the average airline passenger, and you are demonstrably not the average driver, how much of that hundred can you claw back by being careful? Stack the conditionings that have counted denominators, each one in your favour, and watch where the ladder actually stops.