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RichardKennaway comments on Don't You Care If It Works? - Part 1 - Less Wrong
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That is not my understanding of the term "optional stopping" (nor, more significantly, is it that of Jaynes). Optional stopping is the process of collecting data, computing your preferred measure of resultiness as you go, and stopping the moment it passes your criterion for reporting it, whether that is p<0.05, or a Bayes factor above 3, or anything else. (If it never passes the criterion, you just never report it.) That is but one of the large arsenal of tools available to the p-hacker: computing multiple statistics from the data in the hope of finding one that passes the criterion, thinking up more hypotheses to test, selective inclusion or omission of "outliers", fitting a range of different models, and so on. And of these, optional stopping is surely the least effective, for as Jaynes remarks in "Probability Theory as Logic", it is practically impossible to sample long enough to produce substantial support for a hypothesis deviating substantially from the truth.
All of those other methods of p-hacking involve concealing the real hypothesis, which is the collection of all the hypotheses that were measured against the data. It is like dealing a bridge hand and showing that it supports astoundingly well the hypothesis that that bridge hand would be dealt. In machine learning terms, the hypothesis is being covertly trained on the data, then tested on how well it fits the data. No measure of the latter, whether frequentist or Bayesian, is a measure of how well the hypothesis will fit new data.
If you look at the paper, what you call optional stopping is what the authors called "data peeking."
In their simulations, the authors first took in a sample of 20 and calculated it, and then could selectively continue to add data up to 30 (stopping when they reach "effect" or 30 samples). The papers point is that this does skew the Bayes factor (doubles the chances of managing to get a Bayes factor > 3).
It skews the Bayes factor when the hypothesis is in fact not true. The times that the hypothesis is true should balance out to make the calibration correct overall.
In practice what p-hacking is about is convincing the world of an effect, so you are trying to create bias toward any data looking like a novel effect. Stopping rules/data peeking accomplish this just as much for Bayes as for frequentist inference (though if the frequentist knows about the stopping rule they can adjust in a way that bayesians can't), which is my whole point.
Whether or not the Bayesian calibration is overall correct depends not just on the Bayes factor but the prior.
It depends only on the prior. I consider all these "stopping rule paradoxes" disguised cases where you give the Bayesian a bad prior, and the frequentist formula encodes a better prior.
You still wouldn't have more chances of showing a novel effect than you thought you would when you went into the experiment, if your priors are correct. If you say "I'll stop when I have a novel effect", do this many times, and then look at all the times you found a novel effect, 95% of the time the effect should actually be true. If this is wrong, you must have bad priors.
Then you are doing a very confusing thing that isn't likely to give much insight. Frequentist inference and Bayesian inference are different and it's useful to at least understand both ideas(even if you reject frequentism).
Frequentists are bounding their error with various forms of the law of large numbers, they aren't coherently integrating evidence. So saying the "frequentist encodes a better prior" is to miss the whole point of how frequentist statistics works.
And the point in the paper I linked has nothing to do with the prior, it's about the bayes factor, which is independent of the prior. Most people who advocate Bayesian statistics in experiments advocate sharing bayes factors, not posteriors in order to abstract away the problem of prior construction.
Let me put it differently. Yes, your chance of getting a bayes factor of >3 is 1.8 with data peeking, as opposed to 1% without; but your chance of getting a higher factor also goes down, because you stop as soon as you reach 3. Your expected bayes factor is necessarily 1 weighted over your prior; you expect to find evidence for neither side. Changing the exact distribution of your results won't change that.
Should that say, rather, that its expected log is zero? A factor of n being as likely as a factor of 1/n.
My original response to this was wrong and has been deleted
I don't think this has anything to do with logs, but rather that it is about the difference between probabilities and odds. Specifically, the Bayes factor works on the odds scale but the proof for conservation of expected evidence is on the regular probability scale
If you consider the posterior under all possible outcomes of the experiment, the ratio of the posterior probability to the prior probability will on average be 1 (when weighted by the probability of the outcome under your prior). However, the ratio of the posterior probability to the prior probability is not the same thing as the Bayes factor.
If you multiply the Bayes factor by the prior odds, and then transform the resulting quantity (ie the posterior) from the odds scale to a probability, and then divide by the prior probability, the resulting quantity will on average be 1
However, this is too complicated and doesn't seem like a property that gives any additional insight on the Bayes factor..
That's probably a better way of putting it. I'm trying to intuitively capture the idea of "no expected evidence", you can frame that in multiple ways.
Huh? E[X] = 1 and E[\log(X)] = 0 are two very different claims; which one are you actually claiming?
Also, what is the expectation with respect to? Your prior or the data distribution or something else?
I think I understand frequentism. My claim here was that the specific claim of "the stopping rule paradox proves that frequentism does better than Bayes" is wrong, or is no stronger than the standard objection that Bayes relies on having good priors.
What I meant is that you can get the same results as the frequentist in the stopping rule case if you adopt a particular prior. I might not be able to show that rigorously, though.
That paper only calculates what happens to the bayes factor when the null is true. There's nothing that implies the inference will be wrong.
There are a couple different version of the stopping rule cases. Some are disguised priors, and some don't affect calibration/inference or any Bayesian metrics.
That is the practical problem for statistics (the null is true, but the experimenter desperately wants it to be false). Everyone wants their experiment to be a success. The goal of this particular form of p-hacking is to increase the chance that you get a publishable result. The goal of the p-hacker is to increase the probability of type 1 error. A publication rule based on Bayes factors instead of p-values is still susceptible to optional stopping.
You seem to be saying that a rule based on posteriors would not be susceptible to such hacking?
I'm saying that all inferences are still correct. So if your prior is correct/well calibrated, then your posterior is as well. If you end up with 100 studies that all found an effect for different things at a posterior of 95%, 5% of them should be wrong.
So what I should say is that the Bayesian doesn't care about the frequency of type 1 errors. If you're going to criticise that, you can do so without regard to stopping rules. I gave an example in a different reply of hacking bayes factors, now I'll give one with hacking posteriors:
Two kinds of coins: one fair, one 10%H/90%T. There are 1 billion of the fair ones, and 1 of the other kind. You take a coin, flip it 10 times, then say which coin you think it is. The Bayesian gets the biased coin, and no matter what he flips, will conclude that the coin is fair with overwhelming probability. The frequentist gets the coin, get ~9 tails, and says "no way is this fair". There, the frequentist does better because the Bayesian's prior is bad (I said there are a billion fair ones and only one biased one, but only looked at the biased ones).
It doesn't matter if you always conclude with 95% posterior that the null is false when it is true, as long as you have 20 times as many cases that the null is actually false. Yes, this opens you up to being tricked; but if you're worried about deliberate deception, you should include a prior over that. If you're worried about publication bias when reading other studies, include a prior over that, etc.
But that is based on the posterior.
When I ask for clarification, you seem to be doing two things: 1. changing the subject to posteriors 2. asserting that a perfect prior leads to a perfect posterior.
I think 2 is uncontroversial, other than if you have a perfect prior why do any experiment at all? But it is also not what is being discussed. The issue is that with optional stopping you bias the Bayes factor.
As another poster mentioned, expected evidence is conserved. So let's think of this like a frequentist who has a laboratory full of bayesians in cages. Each Bayesian gets one set of data collected via a standard protocol. Without optional stopping, most of the Bayesians get similar evidence, and they all do roughly the same updates.
With optional stopping, you'll create either short sets of stopped data that support the favored hypothesis or very long sets of data that fail to support the favored hypothesis. So you might be able to create a rule that fools 99 out of the 100 Bayesians, but the remaining Baysian is going to be very strongly convinced of the disfavored hypothesis.
Where the Bayesian wins over the frequentist is that if you let the Bayesians out of the cages to talk, and they share their likelihood ratios, they can coherently combine evidence and the 1 correct Bayesian will convince all the incorrect Bayesians of the proper update. With frequentists, fewer will be fooled, but there isn't a coherent way to combine the confidence intervals.
So the issue for scientists writing papers is that if you are a Bayesian adopt the second, optional stopped experimental protocol (lets say it really can fool 99 out of 100 Bayesians) then at least 99 out of 100 of the experiments you run will be a success (some of the effects really will be real). The 1/100 that fails miserably doesn't have to be published.
Even if it is published, if two experimentalists both average to the truth, the one who paints most of his results as experimental successes probably goes further in his career.