Beautiful Probability

"This doesn't mean that probability theory has ceased to apply, any more than your inability to calculate the aerodynamics of a 747 on an atom-by-atom basis implies that the 747 is made out of atoms" should read "... is not made out of atoms."

Eliezer,

I like your essays, but I feel that you are really beating a naive and unsophisticated frequentist straw man (straw person, politically correctly speaking). I think that the answer to the question "Should we draw different conclusions?" depends on some further assumptions about the process and about the type of conclusions we want to make. What kind of frequentist would think that his research is free of subjective assumptions? A naive one.

I admit that I am out of my depth and I would like to know more about Jaynes example.

Erratum: in the comment above, it should say "his or her research" ;)

To answer your story about data:

One person decides on a conclusion and then tries to write the most persuasive argument for that conclusion.

Another person begins to write an argument by considering evidence, analyzing it, and then comes to a conclusion based on the analysis.

Both of those people type up their arguments and put them in your mailbox. As it happens, both arguments happen to be identical.

Are you telling me the first person's argument carries the exact same weight as the second?

In other words, yes, the researcher's private thoughts do matter, because P(observation|researcher 1) != P(observation|researcher 2) even though the observations are the same.

I think that's the proper Bayesian objection, anyway.

95% confidence means that if you repeat the experiment you get the right answer 95% of the time.

That depends on your thoughts because what counts as a success comes up in the repeats.

The experiment itself does not tell you what would have counted as a success. It simply is. No confidence concept applies.

Emil, thanks, fixed.

Doug, your analogy is not valid because a biased reporting method has a different likelihood function to the possible prior states, compared to an unbiased one. In this case the single, fixed dataset that we see, has a different likelihood to the possible prior states, depending on the reporting method.

If a researcher who happens to be thinking biased thoughts carries out a fixed sequence of experimental actions, the resulting dataset we see does not have a different likelihood function to the possible prior states. All that a Bayesian needs to know is the experimental actions that were actually carried out and the data that was actually observed - not what the researcher was thinking at the time, or what other actions the researcher might have performed if things had gone differently, or what other dataset might then have been observed. We need only consider the actual experimental results.

Londenio, see Ron's comment - it's not a strawperson.

Something popped into my mind while I was reading about the example in the very beginning. What about research that goes out to prove one thing, but discovers something else?

Group of scientists want to see if there's a link between the consumption of Coca-Cola and stomach cancer. They put together a huge questionnaire full of dozens of questions and have 1000 people fill it out. Looking at the data they discover that there is no correlation between Coca-Cola drinking and stomach cancer, but there is a correlation between excessive sneezing and having large ears.

So now we have a group of scientists who set out to test correlation A, but found correlation B in the data instead. Should they publish a paper about correlation B?

Doug S., I agree on principle, but disagree on your particular example because it is not statistical in nature. Should we not be hugging the query "Is the argument sound?" If a random monkey typed up a third identical argument and put it in the envelope, it's just as true. The difference between this and the a medical trial is that we have an independent means to verify the truth. Argument screens off Methodology...

If evidence is collected in violation of the fourth amendment rights of the accused, it's inadmissable in court, yes, but that doesn't mean that, ceteris paribus, the prosecution KNOWS LESS than if it were obtained legally.

So, when do I start agreeing with you? Here: The problem lies in the fact that the two trial methodologies create different sorts of Everett branches. The fact that the methodologies differed is ITSELF a piece of evidence which the esteemed Mr. Yudkosky doesn't appear to have room for in this Bayesian analysis. I agree that the relevant post appears to be What Evidence Filtered Evidence?

Hi, Im from Melbourne. All I can say is beware of any organisation or group of people who claim to be committed to over coming bias. Isnt that what all the "true believers" in his-story imagined that they were doing?

Heisenberg, and others told us that the very act of observing anything includes all sorts of unconscious biases which both effect the state of what is being observed, and via feedback, the state of the presumed observer, and of course, the results of any and every research project, no matter what it is. A person stuffed with hambugers obviously perceives everything differently than a Yogi who eats a purifying vegetarian diet, does pranayama (breathing) exercises, and hatha yoga too. The states of their nervous systems would be completely different, and hence their perceptions too. ALL perceptions are electronic fabrications and projections of the brain nervous system complex. We never see the world--only our brain created electronic projections---always, all of the time.

ALL thinking involves a bias---no exceptions. Why are you always thinking any way?

All of that is inevitable when a limited point of view to any act of observation. What is behind your head? What does the room look like from the point of view of your toe nail or from the other end of the room? What does the room look like from every possible point of view within the room? And from every possible point of view in space and time? Where is the room? Where, and who, and what,are you?

How can you explain the authentic world view communicated in the dot paintings of the best Australian so called "aboriginal" artists? It is radically different to our western way of seeing seeing, and yet completely coherent to an "aboriginal", and an integral part/expression of their culture altogether.

Perhaps it is far more real and ALIVE than our impoverished and power seeking objectification power/knowledge games which effectively reduce everything to dead matter---even if Bayesian methods are used.

The search for scientific "knowledge" is really hunter-gatherer behaviour which originates from the very primitive pre-civilized sections of the brain---the reptilian brain.

A quote from Carlos Casteneda.

" In European membership the "world" is built largely from what the eyes report to the mind. In sorcery the total body is used as a receptor. As Europeans we see a "world" out "there" and talk to ourselves about it. We are "here" and the "world" is "there". Our eyes feed our "reason" and we have no direct knowledge of things. According to sorcery this burden on the eyes is unnecessary. We know with the total body."

The only way bias could be truly over come would be to see the world from the Acausal perspective of God's eyes---the room and the universe in its totality before it is cut up into "objectified", and thus controlled. The process of objectifying any and everything is about gaining power and control----the Western gaze! This is what Western "culture" is all about. Power and control.

Woops, looks like I may have shot myself in the foot. The same way argument screens off authority, the actual experiment that was run screens off the intentions of the researcher.

Efficacy of the drug -> Results of the experiment <- Bias of the researcher

Efficacy, Bias -> Results of the experiment -> Our analysis of the efficacy of the drug

Leo: "...the actual experiment that was run screens off the intentions of the researcher."

As long as the validity and reliability of the experiment itself aren't affected by the bias, then the findings are your territory. Analysis is the creation of the map, where all sorts of things can go awry.

Data may be confusing, or even misleading, but this is a fact about us, not the data. Data acquired from valid experiment does not lie, whatever your motives. It might just be telling you something you're not listening to.

"The most exciting phrase to hear in science, the one that heralds new discoveries, is not 'Eureka!' but 'That's funny...'." - Isaac Asimov

Slightly off-topic from the blog, apologies.

I am sorry that I am too lazy to read this thoroughly, but to me the original problem seems a mere illusion and a strawman. A priori, the two experiments are different, but who cares? The experiment with its stopping condition yields a distribution of results only if you have some assumed a priori distribution over the patient population. If you change the stopping condition without changing this distribution, you change the experiment and you get a different distribution for the result. This has nothing to do with evidential impact. Frequentists don't, as far as I can tell, claim anything like that.

I am sorry that I am too lazy to read this thoroughly, but to me the original problem seems a mere illusion and a strawman. A priori, the two experiments are different, but who cares? The experiment with its stopping condition yields a distribution of results only if you have some assumed a priori distribution over the patient population. If you change the stopping condition without changing this distribution, you change the experiment and you get a different distribution for the result. This has nothing to do with evidential impact. Frequentists don't, as far as I can tell, claim anything like that.

Are P(r>70|effective) and P(r>70|~effective) really the same in those two experiments? Trivially, at least, in the second one P(r<60)=0, unlike in the first, so the distribution of r over successive runs must be different. The sequences of experimental outcomes happened to be the same in this case, but not in the counterfactual case where fewer than 60 of the first 100 patients were cured, and it seems that in fact that would affect the likelihood ratio. (I may run a simulation when I have the time.)

Oh, wait: assuming the second researcher stops as soon as (r >= 60) AND (N >= 100) (the latter expression to explain that they kept going until r=70), then the distribution above 60 will actually not be any different (all the probability mass that was in r100, well, only the second experimenter could possibly have generated that result.

Are you telling me the first person's argument carries the exact same weight as the second?

Yes. It's the arguments that matter.

Now, if we know that one person was trying to support a thesis and the other presenting the data and drawing a conclusion, we can weight them differently, if we only have access to one. The first case might leave out contrary data and alternative hypotheses in an attempt to make the thesis look better. We expect the second case to mention all relevant data and the obvious alternatives, if only briefly, so the absence of contrary data is evidence of its nonexistence in that case.

Since we have both, we can exclude the possibility that the first author left out data to make his case look better. Thus, the two arguments are equally valid.

Eliezer_Yudkowsky: As you described the scenario at the beginning ... you're right. But realistically? You need to think about P(~2nd researcher tained the experiment|2nd researcher has enormous stake in the result going a certain way). :-P

It is not completely unreasonable to believe that the big problem in medical research is not a lack of data or a lack of efficient statistical procedures to translate the data into conclusions, but rather the domination of the process by clever arguers. The old-fashioned procedure seems to penalize clever arguers. Although it is of course regrettable that the penalization is an accidental side effect of a misunderstanding of math, the old-fashioned procedure might in fact work better than a procedure whose sole objective is to squeeze as much knowledge from the data as possible.

A good post on a profoundly beautiful subject, and a nice bit of jujutsu the way it works against the backdrop of the meta-commentary.

A minor quibble: Have you considered that use of "Law", like "The Way", while perhaps appropriately elevating, might work against your message by obscuring appreciation of increasingly general "principles"?

For some good mockery of orthodox statistical concepts I recommend the writings of Guernsey McPearson.

Actually never mind, the good parts are harder to find than I thought.

Elizer says:

"We aren't enchanted by Bayesian methods merely because they're beautiful. The beauty is a side effect. Bayesian theorems are elegant, coherent, optimal, and provably unique because they are laws."

This seems deeply mistaken. Why should we believe that bayesian formulations are any more inherently "lawlike" than frequentist formulations? Both derive their theorems from within strict formal systems which begin with unchanging first principles. The fundamental difference between Bayesians and Frequentists seems to stem from different ontological assumptions about the nature of a probability distribution (Frequentists imagine a distribution as a set of possible outcomes which would have occurred under different realizations of our world, whereas Bayesians imagine a distribution as a description of single subjective mental state regarding a single objective world about which we are uncertain).

Moreover, doesn't Cox's Theorem imply that at a sufficient level of abstraction, any Bayesian derivation could (at least in principle) be creatively re-framed as a Frequentist derivation, since both must map (at some level) onto the basic rules of probability? It seems to me, that as far as the pure "math" is concerned, both frameworks have equal claim to "lawlike" status.

It therefore seems that what drives Eliezer (and many others, myself included) towards Bayesian formulations is a type of (dare I say it?) bias towards a certain kind of beauty which he has cleverly re-labeled as "law."

Elizer says:

"We aren't enchanted by Bayesian methods merely because they're beautiful. The beauty is a side effect. Bayesian theorems are elegant, coherent, optimal, and provably unique because they are laws."

This seems deeply mistaken. Why should we believe that bayesian formulations are any more inherently "lawlike" than frequentist formulations? Both derive their theorems from within strict formal systems which begin with unchanging first principles. The fundamental difference between Bayesians and Frequentists seems to stem from different ontological assumptions about the nature of a probability distribution (Frequentists imagine a distribution as a set of possible outcomes which would have occurred under different realizations of our world, whereas Bayesians imagine a distribution as a description of single subjective mental state regarding a single objective world about which we are uncertain).

Moreover, doesn't Cox's Theorem imply that at a sufficient level of abstraction, any Bayesian derivation could (at least in principle) be creatively re-framed as a Frequentist derivation, since both must map (at some level) onto the basic rules of probability? It seems to me, that as far as the pure "math" is concerned, both frameworks have equal claim to "lawlike" status.

It therefore seems that what drives Eliezer (and many others, myself included) towards Bayesian formulations is a type of (dare I say it?) bias towards a certain kind of beauty which he has cleverly re-labeled as "law."

Eliezer,

I'm afraid that I too was seduced by Doug's analogy, and for some reason am a little too slow to follow your response. Any chance you could try again to explain why the analogy doesn't work?

I am by no means an expert in statistics, but I do appreciate Eliezer Yudkowsky's essay, and think I get his point that, given only experiment A and experiment B, as reported, there may be no reason to treat them differently IF WE DON'T KNOW of the difference in protocol (if those thoughts are truly private). But It does seem rather obvious that, if there were a number of independent experiments with protocol A and B, and we were attempting to do a meta-analysis to combine the results of all such experiments, there would be quite a number of experiments where n would be greater than 100 (from protocol B). With the protocol as stated, these would all end when cures were greater than but very close to 60%. If we assume that the "real" cure rate in the population is close to 70%, then, unless some Bayesian term is introduced to account for the bias in methodology, the meta-analysis would seem to be biased toward the incorrect conclusion that the lower 60% figure was closer to reality. Presumably, that kind of bias would be noticed in the experiments with n > 100, and could not have been kept as a private thought with a large number of repeat experiments.

I am not sure, but I would think that, if Bayesian analysis is (or can be) as rigorous as it is claimed, then even the analysis of the original pair might be expected to include some terms that would reflect that potential bias due to a difference in protocol IF THAT DIFFERENCE IS KNOWN to the Bayesian statistician doing the analysis. I find it disturbing that experiment A could have come out to have n = 100 and cure rate = 60%, or n = 1000 and cure rate = 60%, but not with cure rate = 59%, no matter how large n might have become.

I second conchis's request. Shouldn't the second method cut against assumption of a randomized sample?

I'm also thinking of an analogy to the problem of only reporting studies that demonstrate the effectiveness of a drug, even if each of those studies on its own is fair. It seems to me as if stopping when and only when one gets the results one wants is similarly problematic, once again even if everything else about the experiment is strictly ok; outcomes that show 60%+ effectiveness are favored under that method, so P(real effectiveness!=60%|experimental effectiveness=60%) should be increased. Now, I understand why the effect here would be much smaller than in the case of simply leaving out inconvenient data, but I don't understand why I should think that it is exactly equal to zero.

Conchis and Benquo: Eliezer's response to Doug was that the probability of a favorable argument is greater, given a clever arguer, than the prior probability of a favorable argument. But the probability of a 60% effectiveness given 100 trials, given an experimenter who intended to keep going until he had a 60% effectiveness, is no greater than the prior probability of a 60% effectiveness given 100 trials. This should be obvious, and does distinguish the case of the biased intentions from the case of the clever arguer.

To make that claim more obvious: suppose I am involved in the argument between the Greens and the Blues, and after seeing the blue sky, I intend to keep looking up at the sky until it looks green. This won't make it any more probable that when I look at the sky tomorrow, it will look green. This probability is determined by objective facts, not by my intentions, and likewise with the probability of getting a 60% effectiveness from 100 trials.

I just saw an incredibly beautiful sunset. I also see the beauty in some of EY's stuff. Does that mean the sunset was Bayesian, or indeed subject to underlying lawfulness ? No, it only means my enhanced primate brain has a tendency to see beauty in certain things. Not that there is any more epistemic significance in a sunset than there is in a theorem.

I admit that I am still not quite sure what a "Bayesian" is as opposed to and "Old style" statistician (though I am very familiar with Bayes theorem, prior probabilities, likelihood ratios, etc).

That being said, the example at the beginning of the post is a great example of "after the fact" reasoning. If researcher number #2 had required 1,000 trials, then you could say that our interpretation of his results are the same as, say, "researcher #3" who set out to have 1,000 trials no matter how many cures were observed. Since (I would imagine) we would all agree that the conclusion of researcher #3's results are the same (if not stronger) than researcher #1's, than one must come to the conclusion that the interpretation of researcher #1's results are the same as researcher #2's, REGARDLESS of how many trial is takes researcher #2 to get his desired results. And (again, I think) we can all agree that just isn't the case.

I would also like to second Elver's comment above; it is another example of "after the fact" reasoning.

Sort of like shooting, and declaring whatever you hit to be your target.

Had to actually think about it a bit, and I think it comes down to this:

The thing that determines the strength of evidence in favor of some hypothesis vs another is "what's the likelihood we would have seen E if H were true vs what's the likelihood we would have seen E if H were false"

Now. experimenter B is not at all filtering based on H being true or false, but merely the properties of E.

So the fact of the experimenter presenting the evidence E to us can only (directly) potentially give us additional information on the properties of the total evidence E that was collected, rather than (directly) telling us anything about H.

But... the "filtering" rule the experimenter uses is only when to stop experimenting. In other words, once the experimenter does present data E, we know that E is all the evidence there is that he collected. In other words, this isn't filtered evidence in the sense of the experimenter throwing away data he or she doesn't like because once we are given E, there's nothing more to know.

Let me clarify that: Imagine you didn't know the difference in the second experimenter's protocol, you had thought they were the same. Then later you learn the difference. Have you actually learned anything new? Is there any new info about E that you have that you didn't already believe you had?

In this case, no, because unlike filtered evidence situations, the information about the experimenter's intent has no affect on what other possible evidence there may have been that was hidden from you. The probability of you seeing this specific evidence, this specific chunk of data from experimenter A is the same as that from experimenter B, given either effectiveness or non effectiveness.

There're other patterns of data that one would expect to be possible to see from A but not from B, and other patterns that one would expect to possibly see from B but not from A, but these specific data sets being published have probability completely independant of which experimenter was doing it, right?

There are some rather baroque kinds of prior information which would require a Bayesian to try to model the researcher's thought processes. They pretty much rely on the researcher having more information about the treatment effectiveness than is available to the Bayesian, and that the stopping rule depends on that extra information. This idea could probably be expressed more elegantly as a presence or absence of an edge in a Bayesian network, twiddling the d-separation of the stop-decision node with the treatment effectiveness node.

"So now we have a group of scientists who set out to test correlation A, but found correlation B in the data instead. Should they publish a paper about correlation B?"

Since you testing multiple hypotheses simultaneously, it is not comparable to Eliezer's example. Still, it is an interesting question...

Sure. The more papers you publish the better. If you are lucky the correlation may hold in other test populations and you've staked your claim on the discovery. Success is largely based on who gets credit.

Should a magazine publish papers reporting correlations with relatively high P-values? When thousands of scientists are data mining for genetic correlations to disease, chance correlations will be very common. If the genetic difference occurred in a metabolic pathway known to be relevant to the disease, the correlation might be publishable even with a high P-value. If the scientists just reported a random correlation they should have a low P-value.

A better approach might be to replace publication in a journal by some other mechanism. Suppose there were an online, centralized database for hypotheses related to a disease or trait. No single population study would be meaningful, but multiple reports by different researchers in different populations would be significant. Evidence would accumulate and credit would be shared among all those responsible for validating or disproving the hypothesis.

Unknown, I still find it difficult to accept that there should be literally zero modification. It's important not just that n=100, but that n=100 random trials. Suppose both researchers reported 100% effectiveness with the same n, but researcher 2 threw out all the data points that suggested ineffectiveness? You still have an n=100 and a 100% effectiveness among that set, but any probability judgment that doesn't account for the selective method of picking the population is inadequate. I would suggest that either less or a different kind of information is transmitted when the magnitude of n (i.e. the sample size) is not a precondition, and is crafted to enhance a certain outcome. It's a subtler form of "throwing out the data" that doesn't agree with you.

Why isn't this just a much subtler version of the Monty Hall problem? It matters when and how the sample size was selected.

To put it in more concrete terms: if you assume, by hypothesis, that as n increases, the effectiveness percentage will fluctuate randomly due to statistical clustering, in the range between 54 and 61, then there is only an infinitesimal chance that, given truly infinite resources, researcher 2 from the original problem will not come up with the 60% figure, but the chance that researcher 1 will come up with the same figure is significantly less than 100%. If researcher 2 performs his experiment a large enough number of times, the distribution of his "n"s will be described by some kind of probability curve. And you will get 100% confirmation of the 60% figure. Whereas if you assign researcher 1 a priori the same distribution pattern of "n"s, his reported effectiveness percentage will be something like 57.5%. And you could come up with an infinite amount of evidence either way.

Now, of course, in real life the magnitude of n has some upper bound, so researcher 2 is playing a kind of martingale game with the facts, and I don't know enough math to be sure that doesn't precisely cancel out the difference, on average, between his data and that of researcher 1. But then again real life isn't a thought experiment (at least not one we're aware of), and researcher 2 is unlikely to abstain from some other subtle unconscious skewing of the data.

Suppose both researchers reported 100% effectiveness with the same n, but researcher 2 threw out all the data points that suggested ineffectiveness?

Yes, but that is not the case that was described to us.

The mindset of the researchers doesn't matter - only the procedure they follow does. And as unlikely as it may be, in the examples we're provided, the second researcher does not violate the proper procedure.

I have to say, the reason the example is convincing is because of its artificiality. I don't know many old-school frequentists (though I suppose I'm a frequentist myself, at least so far as I'm still really nervous about the whole priors business -- but not quite so hard as all that), but I doubt that, presented with a stark case like the one above, they'd say the results would come out differently. For one thing, how would the math change?

But the case would never come up -- that's the thing. It's empty counterfactual analysis. Nobody who is following a stopping rule as ridiculous as the one offered would be able to otherwise conduct the research properly. I mean, seriously. I think Benquo nailed it: the second researcher's stopping rule ought to rather severely change our subjective probability in his/her having used a random sample, or for that matter not committed any number of other research sins, perhaps unconsciously. And that in turn should make us less confident about the results.

Uh, strike the "how would the math change?" question -- I just read the relevant portion of Jaynes's paper, which gives a plausible answer to that. Still, I deny that an actual practicing frequentist would follow his logic and treat n as the random variable.

(ALSO: another dose of unreality in the scenario: what experimenter who decided to play it like that would ever reveal the quirky methodology?)

Maybe in private notes?

And as far as thinking that N was the random variable in the second case, I had, I'd thought it through, and basically concluded that since no data at all was being hidden from us by experimenter B, and since A and B followed the same procedure, the probability that specific outcome would be published by B was the same as that of A

now, there is a partial caveat. One might say "but... What if B's rule was to only publish the moment he had at least 70%?"

So one might think there's more possible ways it could have come out like that for A then B, so that may affect things..

But no, and there's two ways to look at it...

One is if you ask "what is the Specific data A has?", ie, not just cures out of total trials, but the specific outcome of each patient, the likelihoods would then correspond to one specific outcome. And since the trials are (assumed) independant of each other given that the effectiveness of the medication is held fixed, rearanging the patients doesn't alter the likelihood. So they can be rearranged to match B's data without changing anything, even if we know B's data must have the property that the 100th trial was the first one to get to 70% or above.

So, what happens here.. you know that no matter what answer you get to the question "what, precisely, was A's data", the produced likelihoods would then end up being identical to the likelihood produced from B's data.

ie, by the principle of expectation of future belief has to equal present belief, you've gained same knowledge from both.

Another way to look at it is to consider that the only difference between the two, under these assumptions, would be a combinatorial coefficient. And that would be independant of the effectiveness itself given the numbers of how many cures vs non cures.

So that'll cancel out when computing the likelihood ratios.

Paul Gowder,

You've read Jaynes -- now read MacKay.

"Information Theory, Inference, and Learning Algorithms" (available for download here).

The key portions are sections 37.2 - 37.3 (pp 462-465).

Cyan, excellent link!

Caledonian,

I agree that the two cases are not precisely the same. I also agree that they are not, as a matter of degree, very close. But it seems to me that stopping at a desired result is implicitly the same as "throwing out" other possible results, if the desired result is one of the several results possible in the range of all feasible "n"s. In other words, what I meant by my "more concrete" example is that researcher 2's experiment is properly a member of the set of all possible type-2 experiments (all of which will produce 60%+), while researcher 1's experiment is one of the set of all possible type-1 experiments which may well produce a different number.

The method of selecting "n" matters. Look at Bertrand's paradox for a mathematical example: http://en.wikipedia.org/wiki/Bertrand%27s_paradox_%28probability%29 P(60% cured|n=100) is not the same thing as P(n=100|60% cured).

On the other hand, it might be that Mr. Yudkowsky mean us to read r=70 as implying that n=100 was the minimum n. In that case, provided we know researcher 2 didn't throw out another n=100 data set that he didn't like, I can see why the examples are equivalent; only once researcher 2 expands the data set are we to be suspicious. A good heuristic, then, might be in such cases to only look at the first n = "minimum number of data points" cases. This could save otherwise useless data.

I had assumed from the description of researcher 2's motives (as I think others did) that he performed the minimum number of tests to get the desired result, and that r=70/100 was offset by the control group.

But it seems to me that stopping at a desired result is implicitly the same as "throwing out" other possible results

You did not speak about throwing out possible results. You spoke of throwing out data that went against the desired conclusion.

These are very, very different actions, with different implications.

Cyan, that source is slightly more convincing.

Although I'm a little concerned that it, too, is attacking another strawman. At the beginning of chapter 37, it seems that the author just doesn't understand what good researchers do. In the medical example given at the start of the chapter (458-462ish), many good researchers would use a one-sided hypothesis rather than a two-sided hypothesis (I would), which would better catch the weak relationship. One can also avoid false negatives by measuring the power of one's test. McKay also claims that "this answer does not say how much more effective A is than B." But that's just false: one can get an idea of the size of the effect with either sharper techniques (like doing a linear regression, getting beta values and calculating r-squared) or just by modifying one's null hypothesis (i.e. demanding that a datum improve on control by X amount before it counts in favor of the alternative hypothesis).

Given all that, I'm going to withhold judgment. McKay's argument on the coin flip example is convincing on the surface. But given his history from the prior pages of understating the counterarguments, I'm not going to give it credence until I find a better statistician than I to give me the response, if any, from a "sampling theory" perspective.

It's worth noting that hypothesis testing as it's normally taught is a messy, confused hybrid of two approaches (Fischer and Neyman/Pearson), each of which is individually somewhat more elegant (but still doesn't make philosophical sense):

http://ftp.isds.duke.edu/WorkingPapers/03-26.pdf

http://marketing.wharton.upenn.edu/ideas/pdf/Armstrong/StatisticalSignificance.pdf

Caledonian,

I guess "the same" was a bit of an unintentional exaggeration. I will try to be precise. What I meant was, same in an important way -- that is, likewise excluding only a kind of counterexample.

Paul Gowder,

I agree with you that MacKay's Chi-squared example fails to criticize frequentist best practice. That said, all of the improvements you suggest seem to me to highlight the problem -- you have lots of tools in the toolbox, but only training and subjective experience can tell you which ones are most appropriate. On the question of "which approach is more subjective?", the frequentist advantage is illusory. (On the question of "which approach has the best philosophical grounding?" I go with the Cox theorems.)

Cyan, I've been mulling this over for the last 23 hours or so -- and I think you've convinced me that the frequentist approach has worrisome elements of subjectivity too. Huh. Which doesn't mean I'm comfortable with the the whole priors business either. I'll think about this some more. Thanks.

As a full-blown Bayesian, I feel that the bayesian approach is almost perfect. It was a revelation when I first realized that instead of having this big frequentist toolbox of heuristics, one can simply assume that every involved entity is a random variable. Then everything is solved! But then pretty quickly I came to the catch, namely that to be able to do anything, the probability distributions must be parameterized. And then you start to wonder what the pdf's of the parameters should be, and off we go into infinite regress.

But the biggest catch is of course that the integral for the posterior is almost never solvable. If that wasn't the case, I believe we would have had superhuman AI a long time ago. Still, I think bayesian methods are underexploited in AI. For example, it is straight-forward to make a "curious" system that asks the user all the things it is uncertain of, in a way that minimizes the need for human input (My lab is currently working on such a system for auditory testing).

"Two medical researchers use the same treatment independently [...] one had decided beforehand [...] he would stop after treating N=100 patients, [...]. The other [...] decided he would not stop until he had data indicating a rate of cures definitely greater than 60%, [...]. But in fact, both stopped with exactly the same data: n = 100 [patients], r = 70 [cures]. Should we then draw different conclusions from their experiments?"

[...]

If Nature is one way, the likelihood of the data coming out the way we have seen will be one thing. If Nature is another way, the likelihood of the data coming out that way will be something else. But the likelihood of a given state of Nature producing the data we have seen, has nothing to do with the researcher's private intentions. [...]

The expectations and the stopping rule make a difference. The reason the Monty Hall Puzzle turns out the way it does is that part of the setup is that Monty Hall always opens a different door than you chose. When I tell the story without mentioning that fact, you should get a different answer.

"If anyone should ever succeed in deriving a real contradiction from Bayesian probability theory [...] then the whole edifice goes up in smoke. Along with set theory, 'cause I'm pretty sure ZF provides a model for probability theory."

If you think of probability theory as a form of logic, as Jaynes advocates, then the laws and theorems of probability theory are the proof theory for this logic, and measure theory is the logic's model theory, with measure-theoretic probability spaces (which can be defined entirely with ZF, as you suggest) being the models.

We have additional information about researcher 2's experiment. If researcher 2 didn't look at the data before that point, then the procedures were the same, so the data should be treated the same.

If researcher 2 did check the data along the way--a reasonable enough assumption, given researcher 2's goal--then there were other tests which all came out below 60%. There was an upswing in successes at the end, and we know it. The other experiment may well have experienced the same thing, but in experiment 2, I don't have to look; I see it. Was there an important variable that we overlooked?

Of course, this is only due to extra information I happen to have about the latter. I haven't bothered to check whether something similar was there for the previous, because there wasn't anything to make it catch my attention. If I have the tools to do so, I would still like to treat them both the same--I want to see researcher 1's results lined up by time as well. If the upswing is repeated...well, that's funny.

Eliezer, I accept your point about the underlying laws of probability. However, your example is extremely flawed.

Of course what the researcher operates by should affect our interpretation of the evidence; it is, in itself, another piece of evidence! Specifically in this case, publishing your research only when you reach a certain conclusion implies that any similar researches that did not reach this threshold did not get published, and are thus not available to our evidence pool. This is filtered evidence.

So without knowing how many similar researches were conducted, the conclusion from the one research that did get published can't be seen as very strong. Do I need to draw the Bayesian analysis that shows why?

Should we then draw different conclusions from their experiments?

I assume you mean if you only saw one of them (knowing the researcher's intentions ineither case)? In that case, I would say yes. For the first, the N is random, while for the second N is the smallest N were r>=60. In the second case, the question is: what is the probability that the cure rate will ever reach 60%, while the first case answers the Q: what is the cure rate probability accoding to a sample on N=100

Yes, I would say, draw very differenct conclusions since you ar answering very different questions!

If there is a difference, it is not because the experiments went differently, it is because the experiments could have gone differently, and so the likelihoods of them happening the way they did happen is different.

The Monty Hall problem was mentioned above. I pick a door, Monty opens a door to reveal a goat, I can stick or switch (but can't take the goat). Whether Monty is picking a random door or picking the door he knows doesn't have the goat, the evidence is the same - Monty opened a door and revealed a goat. But if Monty what matters is what might have happened otherwise. If Monty always picks a door with a goat, then I win if I switch 2/3 of the time. If Monty might have picked the door with the car (and just happened not to), I win if I switch only 50% of the time.

Same evidence, different conclusions based solely on what someone might have done otherwise not based on what actually happened; and I am confident of the difference in the Monty Hall problem, as I have not only read about it but also simulated it.

In the situation given, Researcher 1 did stop at 100 experiments, but might have stopped at 49, or 280. Researcher 2 was sure to stop at 100. I am not unwilling to accept that this doesn't change the meaning of the evidence, in this case, but I do not understand at all why it should be "obvious" that it can't, given that it does in the case of the Monty Hall problem.

I was confused by this post for some time, and I feel I have an analagous but clearer example: Suppose scientist A says "I believe in proposition A, and will test it at the 95% confidence level", and scientist B says "I believe in proposition B, and will test it at the 99% confidence level". They go away and do their tests, and each comes back from their experiment with a p-value of 0.03. Do we now believe proposition A more or less than proposition B? The traditional scientific method, with its emphasis on testability, prefers A to B; for a bayesian it's clear that we have the same amount of evidence for each.

Have I fairly characterised both sides? Does this capture the same paradox as the original example, and is it any clearer?

Tentatively, I think we must treat the two differently, in some respect somewhere, or we are vulnerable to manipulation. Where does the flaw lie in the following?

If the second researcher had instead said, "I am going to run 1000 experiments with 100 people each, and publish only those whose cure rate exceeds 60%", there is a huge selection bias in the data we see and our update should be tiny if we can't get access to the discarded data.

If the researcher decided instead "I am going to run 1000 experiments in parallel, adding one person at a time to each, and publish only those whose cure rate exceeds 60%," then we would still see the same sort of bias in the data - after he has added 100 people to each experiment we are in the same situation as above.

If 1000 researchers, ideologically aligned in their commitment to this result, run experiments where they post their results when the cure rate exceeds 60%, this is equivalent to the second scenario.

Therefore, if enough people behaved like researcher 2, we would see biases in published data (which may conceivably balance out, with enough difference in ideology, but this does not seem to be guaranteed and I am not convinced it is even likely).

Therefore, researcher 2 should be considered to be acting badly, and we should reject (or at least weaken) experiments done in that fashion.

The above assumes that we do not see data from in-progress experiments. If we do, then I believe we can safely consider each data point with the same weight.

The argument that confused me at first was: "Wouldn't the second researcher always be able to produce a >60% result given enough time and resources, no matter what the actual efficacy of the treatment is?"

But this is not true. If the true efficacy is < 60%, then the probability of observing a ">60%" result at least once in a sequence of N experiments does not tend to 1 as N goes to infinity.

In the real world, Eliezer's example simply doesn't work.

In the real world you only hear about the results when they are published. The prior probability of the biased researcher publishing a positive result is higher than the prior probability of the unbiased researcher publishing a positive result.

The example only works if you are an omniscient spy who spies on absolutely all treatments. It's true that an omniscient spy should just collate all the data regardless of the motivations of the researcher spied upon. However unless you are an omniscient spy you do need to take into account how an agent showing you new data went about gathering the data that they are showing you. Otherwise you are vulnerable to being "mushroomed" and updating yourself into beliefs that will cause you to lose.

Elezier:

The results of the two experimenters in the example are different: to begin with, the 2nd experimenter's first result is a non-cure (otherwise he would have stopped there with a 100% success); one of the three following results is also a non-cure (otherwise he would have stopped with a 75%); etc. Also, his last result is a cure (otherwise he would have stopped one patient earlier).

The first experimenter certainly got different results -- or you may as well win the lottery: the odds that a Bernoulli trial produces a sequence x1..x100 in which no prefix x1...xN has a higher rate of successes than the whole sequence are really small.

Note that this argument gets weaker as you change the definition of "definitely greater than 60%" to require greater statistical confidence (indeed .99 results are less sensible to methodological biases than .95 results), but even at .99 the odds that the sequence obtained by the 1st doctor would finish exactly where the 2nd doctor would stop are well below 1/10th (I just made a quick upper bound calculation, it is actually even smaller).

The problem is that (1) when the results are reported in a journal, you only get the total counts -- which hides the methodological trap, and (2) even if you got the full results, you most likely don't have the computational power to discover the difference (except of course in the ~60% of reports from doctor 2 where he reports on a single patient).

I don't feel sufficiently comfortable with statistics to tear apart the given example. I do have a different example with which to refute the point that the evidential impact of a fixed set of data should be independent of the researchers prior private thoughts.

Suppose I have two researchers, both looking at the correlations between acne and colored jelly beans. Alfred does twenty tests each with X subjects. Each test will feed subjects jelly beans of a single color for a week and then look at incidences of acne. Boris theorizes that green jelly beans are correlated with acne. Boris then does twenty test each with X subjects, identical to Alfred's test.

Alfred and Boris each use the exact same experimental procedure and each get the exact same results, finding higher rates of acne in subjects fed green jelly beans than in subjects fed other colored jelly beans. Boris' experiment is stronger evidence for a link between green jelly beans and acne than Alfred's experiment. Why? Because coincidences happen all the time.

Boris was looking for a correlation between green jelly beans and acne and the odds that Boris would find a correlation between green jelly beans and acne (by chance alone) was very low. Alfred was looking for a correlation but he wasn't specific about what correlation he was looking for. By chance alone, he was just as likely to find a correlation between blue jelly beans, or red jelly beans, or any of the 17 other colors in the experiment. The fact that this experiment happened to show higher rates with green jelly beans isn't worth very much evidence. Now if Alfred were to use this experiment to form a hypothesis that green jelly beans were correlated with acne and perform another experiment which ALSO showed a relationship between green jelly beans and acne, THEN he would have much stronger evidence.

Jelly beans inspired by XKCD: http://xkcd.com/882/

Having written this out, I'll offer a simpler example. Charlie and David each have a six sided die. They both think his die is weighted. Charlie says "I think this die will land '6' when I roll it". He rolls the die and it lands '6'. David just rolls the die and it lands '6'. They both now believe that his die will always land '6'. Exact same evidence. Charlie is more justified in his belief that the die is weighted to land '6' because if his die was not weighted, there would only be a 1/6 chance that he would have rolled a '6'. If David's die was not weighted, there would be a 6/6 chance that his die would roll to SOMETHING and generated his belief.

When evaluating the rational evidential impact of the results of an experiment, it is imperative that you take into account what it is that is being tested, and that is something that only exists in the experimenters private thoughts (or notebook or whatnot).

If you have twenty minutes, I would recommend this portion of a Radiolab broadcast about coincidences: http://www.radiolab.org/2009/jun/15/a-very-lucky-wind/

I think you're misunderstanding probability theory a little. Probability theory is the chance that x result means that the universe operates on principle y. The fact that the second researcher had no reason to stop until he tested 100 people means that the % of patients cured did not exceed 60% until his last batch of test subjects. Which significantly alters the chance that the universe operates on principle y. The first researcher could have had a % over 60 at any time during the experiment. Which is a physical difference. The probability used is not based on the researcher's private thoughts, it is based on their experimental procedure, which is different, regardless of the fact they ended with the same results.

Old School statisticians thought in terms of tools, tricks to throw at particular problems.

This reminds me of a joke posted on a bulletin board in the stats department at UC Riverside. It was part of a list of humorous definitions of statistical terms. For "confidence interval," it said that the phrase uses a particular, euphemistic meaning of the word "interval;" that meaning could be used to construct similar phrases such as "hat interval," "card interval," or "interval or treat."

And yet... should rationality be math? It is by no means a foregone conclusion that probability should be pretty. The real world is messy - so shouldn't you need messy reasoning to handle it?

And in a way, you do, even doing Bayesian statistics. The messiness is just in the actual numerical calculations, not in the definitions of the rules.

Suppose you're trying to find a good model for some part of the real world, and you've got your set of models you're considering. When you see data, and you use Bayes' Theorem to find the posterior probabilities, the expression is going to have in it P(data|m) for each model m, and P(data). And if your models are messy - necessary to represent a messy real world - then these are going to be complicated expressions that make for a really awful calculation.

So Bayesian statisticians have a toolbox for approximating posterior probabilities - Laplace approximation, Gibbs sampling, etc - to deal with that messiness.

(these are my impressions from a bit of reading of the Bayesian statistics literature - I've never actually done these things, I don't know what the expressions really look like)

"Bayesianism's coherence and uniqueness proofs cut both ways. Just as any calculation that obeys Cox's coherency axioms (or any of the many reformulations and generalizations) must map onto probabilities, so too, anything that is not Bayesian must fail one of the coherency tests. This, in turn, opens you to punishments like Dutch-booking (accepting combinations of bets that are sure losses, or rejecting combinations of bets that are sure gains)."

I've never understood why I should be concerned about dynamic Dutch books (which are the justification for conditionalization, i.e., the Bayesian update). I can understand how static Dutch books are relevant to finding out the truth: I don't want my description of the truth to be inconsistent. But a dynamic Dutch book (in the gambling context) is a way that someone can exploit the combination of my belief at time (t) and my belief at time (t+1) to get something out of me, which doesn't seem like it should carry over to the context of trying to find out the truth. When I want to find the truth, I simply want to have the best possible belief in the present -- at time (t+1) -- so why should "money" I've "lost" at time (t) be relevant?

Perhaps I simply want to avoid getting screwed in life by falling into the equivalents of Dutch books in real, non-gambling-related situations. But if that's the argument, it should depend on how frequently such situations actually crop up -- the mere existence of a Dutch book shouldn't matter if life is never going to make me take it. Why should my entire notion of rationality be based on avoiding one particular -- perhaps rare -- type of misfortune? On the other hand, if the argument is that falling for dynamic Dutch books constitutes "irrationality" in some direct intuitive sense (the same way that falling for static Dutch books does), then I'm not getting it.

Incidentally, Eliezer, I don't think you're right about the example at the beginning of the post. The two frequentist tests are asking distinct questions of the data, and there is not necessarily any inconsistency when we ask two different questions of the same data and get two different answers.

Suppose A and B are tossing coins. A and B both get the same string of results -- a whole bunch of heads (let's say 9999) followed by a single tail. But A got this by just deciding to flip a coin 10000 times, while B got it by flipping a coin until the first tail came up. Now suppose they each ask the question "what is the probability that, when doing what I did, one will come up with at most the number of tails I actually saw?"

In A's case the answer is of course very small; most strings of 10000 flips have many more than one tail. In B's case the answer is of course 1; B's method ensures that exactly one tail is seen, no matter what happens. The data was the same, but the questions were different, because of the "when doing what I did" clause (since A and B did different things). Frequentist tests are often like this -- they involve some sort of reasoning about hypothetical repetitions of the procedure, and if the procedure differs, the question differs.

If we wanted to restate this in Bayesian terms, we'd have to do so by taking into account that the interpreter knows what the method is, not just what the data is, and the distributions used by a Bayesian interpreter should take this into account. For instance, one would be a pretty dumb Bayesian if one's prior for B's method didn't say you'd get one tail with probability one. The observation that's causing us to update isn't "string of data," it's "string of data produced by a given physical process," where the process is different in the two cases.

(I apologize if this has all been mentioned before -- I didn't carefully read all the comments above.)

I believe the example in this post is fundamentally flawed. Some of the other commenters have hinted at the reasons, but I want to add my own thoughts on this.

Before we go into the difference between the frequentist and the Bayesian approach to the problem, we first have to be clear about whether the investigators acknowledge publicly that they use different stopping rules. I am going to cover both cases.

If the stopping rule is not publicly acknowledged, the frequentist data analyst can not take it into account. He will therefore have to use the same tests on the two datasets. Therefore, if experiment one rejects the null hypothesis, so will experiment two.

If the stopping rule is known to the public, a frequentist statistician will appropriately take this into account in his data analysis. As Eliezer says, experiment one may be statistically significant and experiment two may be non-significant. And this is completely appropriate; any rational Bayesian would do essentially the same thing:

Let "A" be the event that somebody publishes a study showing that the drug works in 60% of people. Let "B" be the prior probability that the drug works in at least 60% of people, and let "C" be the biased stopping rule.

In the case of the first investigator, the appropriate likelihood ratio is Pr(A | B) / Pr(A| not B)

In the case of the second investigator, the appropriate likelihood ratio is Pr(A| B, C) / Pr(A| C, not B)

Pr(A | B) / Pr(A| not B) is strictly larger than Pr(A| B, C) / Pr(A| C, not B)

Any Bayesian agent who uses Pr(A | B) / Pr(A| not B) in the case of the second investigator, is throwing away important evidence, namely that a biased stopping rule was applied.

You know what really helps me accept a counterintuitive conclusion? Doing the math. I spent an hour reading and rereading this post and the arguments without being fully convinced of Eliezer's position, and then I spent 15 minutes doing the math (R code attached at the end). And once the math came out in favor of Eliezer, the conclusion suddenly doesn't seem so counterintuitive :)

Here we go, I'm diving all the numbers by five to make the code work but it's pretty convincing either way.

• The setup - Researcher A does 20 trials always, researcher B keeps doing trials until the ratio of cures is at least 70% (1 cure / 1 trial is also acceptable).
• E - The full evidence, namely that 20 patients were tried and 14 were cured.
• H0 - The hypothesis that the success rate of the cure is 60%.
• H1 - The hypothesis that the success rate is 70%.
• Pa - Researcher A's probabilities.
• Pb - Researcher B's probabilities.

In this setup, it's clear to see that Pa and Pb aren't equal for every thing you want to measure. For example, for any evidence E that doesn't contain 20 observations Pa(E)=0. However, Reverend Bayes reminds us that the strength of our EVIDENCE depends on the odds ratio, and not on all the sub probabilities:

P(H1|A) / P(H0|B) = P(H1)/P(H0) P(E|H1)/P(E|H0) aka posterior odds = prior odds odds ratio of evidence. Assuming that the prior odds are the same, let's calculate the odds ratio for both Pa and Pb and see if they are different.

Pa(E|H0) = 12.4%, as a simple binomial distribution: dbinom(14,20,0.6). Pa(E|H1) = 19.1%. The odds ratio: Pa(E|H1)/Pa(E|H0) = 1.54. That's the only measure of how much our posterior should change. If originally we gave each hypothesis an equal chance (1:1), we now favor H1 at a ratio of 1.54:1. In terms of probability, we changed our credence in H1 from 50% to 60.6%.

What about researcher B? I simulated researcher B a million times in each possible world, the H0 world and the H1 world. In the H0 world, evidence E occurred only 5974 times out of a million, for Pb(E|H0) = 0.597% which is very far from 12.4%. It makes sense: researcher 2 usually stops after the first trial, and occasionally goes on for zillions! What about the H1 world? Pb(E|H1) = 0.919%. The odds ratio: Pb(E|H1) / Pb(E|H0) = wait for it = 1.537. Exactly the same!

I think all the other posts explain quite well why this was obviously the case, but if you like to see the numbers back up one side of an argument, you got 'em. I personally am now converted, amen.

R code for simulating a single researcher B:

resb<-function(p=0.6){

cures<-0

tries<-0

while(tries < 21) { # Since we only care whether B stops after 20 trials, we don't need to simulate past 21.

tries<-tries+1

cures<-cures+rbinom(1,1,p)

if((cures/tries) >= 0.7) return(tries)

}

tries }

R code for simulating a million researchers B in H1 world:

x<-sapply(1:1000000,function(i) {resb(0.7)})

length(x[x==20])

This example needs to be refined, two experiments do not produce the same data, second one has different probability space and additional data point - stopping position, and computing probabilities you should also condition on that stopping point N, fact that this N is screened by other data is nontrivial and waiving it just on assumption of beauty could lead to mistake.

It turned out that in this case that is correct move, but could be a mistake quite easily.

Fixing my predictions now, before going to investigate this issue further (I have Mackay's book within the hand's reach and would also like to run some Monte-Carlo simulations to check the results; going to post the resolution later): 

a) It seems that we ought to treat the results differently, because the second researcher in effect admits to p-hacking his results. b) But on the other hand, what if we modify the scenario slightly: suppose we get the results from both researchers 1 patient at a time. Surely we ought to update the priors by the same amount each time? And so by the time we get the 100th individual result from each researcher, the priors should be the same, even if we then find out that they had different stopping criteria.

My prediction is that argument a) turns out to be right and argument b) contains some subtle mistake. 

Interesting article. The Carnot engine, real car and the second law simile is unfortunate. The second law of thermodynamics applies to every physical system (a real car included). The Carnot engine is an idealization of an engine that obeys the laws of thermodynamics. A real engine DOES obey the second law of thermodynamics. It is just not as efficient as the idealized Carnot engine.

The second law gives an upper bound to the efficiency of physical processes. Not that that is the expected efficiency of a real system.

As long as the reputation doctor had committed to publishing the results regardless of what he found, then, yes, the data has equal evidential weight.

However, the story seems to imply he would have continued testing indefinitely until he got it right, and if he didn't, he would have faded into obscurity.

The issue here is that we must SEE the data in the possible world where he has a 58% cure rate with N=1000 (kept trying, kept trying, kept trying, eventually published), if we are to accept his 70/100 results in this world.

If, on the other hand, we would only see the 70/100, but wouldn't have seen the 580/1000, then the 70/100 does not carry the same weight as the other doctor's 70/100.

Imagine a world where the true success rate is 58%. We have 1000 biased researchers all doing the experiment and not publishing when they get 580/1000. The few who get lucky and get a 70/100 publish, leading to the 70%+ success rate results being very over-represented in the data we see.

RE "Should we then draw different conclusions from their experiments?"

I think, depending on the study's hypothesis and random situational factors, a study like the first can be in the garden of forking paths. A study which stops at n=100 when it reaches a predefined statistical threshold isn't guaranteed to have also reached that statistical threshold if it had kept running until n=900.

Suppose a community of researchers is split in half (this is intended to match the example in this article but increase the imagined sample size of studies to more than 1 study and its replication). The first half (non-replicators) of researchers conducts research as mentioned first in the article: they predefine a statistical threshold and stop the study when that threshold is reached. Additionally, if the threshold is not reached when n=1000, then the negative result of the study is published. The second half (replicators) of researchers only do replications of the first half's work, with the same sample size. 

After the studies are done, in some cases, a non-replicator study will find a result and replicator study will find the opposite. In such cases, who is more likely to be correct? I think this article implies that the answer would be 50%, because it is supposedly the same study repeated twice. I do not think that is correct, I think the replicators are correct more than 50% of the time, because the non-replicator studies can be in the garden of forking paths.

The first section of this article explains the general idea of how early stopping can lead to bias: https://www.statisticsdonewrong.com/regression.html

My attempt to be more specific and somewhat mathematical:

For all studies, if we calculate the statistical result of a study for every n, then as n increases, the statistical result may or may not converge monotonically (for almost any study it will converge to something, since reality has regularities, but not necessarily monotonically). Rather, randomness can affect results and the statistical result can bounce a bit up and down between different n. In the case of the non-replicator researchers, for every n, the study can either continue or end, and those 2 options are 2 different paths in the garden of forking paths. If a study's results do not converge monotonically as n increases, then there may be outliers for certain specific n, where for a specific n (or a minority of n), the result of the study does pass the statistical threshold, but for all other n, it would not pass the statistical threshold.

'Nonmonotonic convergence' describes which studies are affected by the early stopping bias. 

Post-script: If a study converges monotonically, then there is no problem with early stopping. However, even if your study had been converging monotonically for every previous n, that isn't an absolute guarantee that it would have continued converging monotonically as n increases. However, the larger the sample size, the larger your confidence.

That's the fundamental difference in mindset. Old School statisticians thought in terms of tools, tricks to throw at particular problems. Bayesians - at least this Bayesian, though I don't think I'm speaking only for myself - we think in terms of laws.

I never realized that until re-reading this many years later. Very cool.