You never count your results, when you're sitting at the lab bench, there will be time enough for counting, when the experiments are done.
(And TIL, this wasn't original to Kenny Rogers!)
Every gambler knows
That the secret to survivin'
Is knowin' what to throw away
And knowin' what to keepIt's easy to create a dogshit null hypotheses by negligence or by "negligence" and it's easy to reject a dogshit null hypothesis by simply collecting enough data as it automatically crumbles on contact with the real world -- that's what makes it dogshit. One might hope that this would be caught by peer review (insist on controls!) but I see enough dogshit null hypotheses roaming around the literature that these hopes are about as realistic as fairy dust. In practice, the dogshit null hypothesis reins supreme, or more precisely it quietly scoots out of the way so that its partner in crime, the dogshit alternative hypothesis, can have an unwarranted moment in the spotlight.
Would you mind giving an example(s) of such and how it differs from a "good" null hypothesis?
So for example, suppose you want to detect if there's unusual patterns in website traffic -- a bot attack or unexpected popularity spike. You look at page views per hour over several days, with the null hypothesis that page views are normally distributed, with constant mean and variance over time.
You run a test, and unsurprisingly, you get a really low p-value, because web traffic has natural fluctuations, it's heavier during the day, it might be heavier on weekends, etc.
The test isn't wrong -- it's telling you that this data is definitely not normally distributed with constant mean and variance. But it's also not meaningful because it's not actually answering the question you're asking.
...but the data table shows a clear trend over time across both groups because the samples were being irradiated by intense sunlight from a nearby window. The model didn't account for this possibility, so it was rejected, just not because the treatment worked.
That's a relatively trivial example and you can already imagine ways in which it could have occurred innocently and not-so-innocently. Most of the time it isn't so straightforward. The #1 culprit I see is failure to account for some kind of obvious correlation, but the ways in which a null hypothesis can be dogshit are as numerous and subtle as the number of possible statistical modeling mistakes in the universe because they are the same thing.
This logic was used repeatedly, but it fails to account for numerous obvious biases. For instance unvaccinated people are generally going to be less proactive in seeking medical treatment, and so the average severity of a case that causes them to go to the hospital is going to be substantially greater than for a vaccinated individual, with an expectation of correspondingly worse overall outcomes. It's not like this is some big secret - most papers mentioned this issue (among many others) in the discussion, but ultimately made no effort to control for it.
"State X saw a mortality rate last year that was statistically significantly higher than the national rate. We should focus our intervention there."
The null hypothesis is that the risks of death are exactly the same in the state vs the nation. That may work with experimental sample sizes, but at the population level you'll often have massive sample sizes. A statistically significant difference is not interesting by itself. It's just the first hurdle to jump before even discussing the importance of the difference. But I've seen publications (especially data reports with sprinklings of discussion) focus entirely on statistical significant differences in narrative next to tables.
This isn't P-hacking an experiment, but it is abusing and misunderstanding statistical significance to make decisions.
> The problem with p-hacking is not the "hacking," it’s the "p." Or, more precisely, the problem is null hypothesis significance testing, the practice of finding data which reject straw-man hypothesis B, and taking this as evidence in support of preferred model A.
https://statmodeling.stat.columbia.edu/2021/09/30/the-proble...
See also this post from 2014 with a discussion of Confirmationist and falsificationist approaches to reasoning in science: https://statmodeling.stat.columbia.edu/2014/09/05/confirmati...
> I understand falisificationism to be that you take the hypothesis you love, try to understand its implications as deeply as possible, and use these implications to test your model, to make falsifiable predictions. The key is that you’re setting up your own favorite model to be falsified.
> In contrast, the standard research paradigm in social psychology (and elsewhere) seems to be that the researcher has a favorite hypothesis A. But, rather than trying to set up hypothesis A for falsification, the researcher picks a null hypothesis B to falsify and thus represent as evidence in favor of A.
> As I said above, this has little to do with p-values or Bayes; rather, it’s about the attitude of trying to falsify the null hypothesis B rather than trying to trying to falsify the researcher’s hypothesis A.
> Take Daryl Bem, for example. His hypothesis A is that ESP exists. But does he try to make falsifiable predictions, predictions for which, if they happen, his hypothesis A is falsified? No, he gathers data in order to falsify hypothesis B, which is someone else’s hypothesis. To me, a research program is confirmationalist, not falsificationist, if the researchers are never trying to set up their own hypotheses for falsification.
> That might be ok—maybe a confirmationalist approach is fine, I’m sure that lots of important things have been learned in this way. But I think we should label it for what it is.
See also: Andrew Gelman and Eric Loken's 2014 "garden of forking paths" paper: https://sites.stat.columbia.edu/gelman/research/unpublished/...
> Running experiments until you get a hit
Is that it's literally what us software optimization engineers do. We keep writing optimizations until we find one that is a statistically significant speed-up.
Hence we are running experiments until we get a hit.
The only defense I know against this is to have a good perf CI. If your patch seemed like a speed-up before committing, but perf CI doesn't see the speed-up, then you just p-hacked yourself. But that's not even fool proof.
You just have to accept that statistics lie and that you will fool yourself. Prepare accordingly.
No, UIs churn because when they get good and stay that way, PMs start worrying no one will remember what they're for. Cf. 90% of UI changes in iOS since about version 12.
And software ultimately fails at perfect composability. So if you add code that purports to be an optimization then that code most likely makes it harder to add other optimizations.
Not to mention bugs. Security bugs even
Say I’m after p<0.05. That means that if I try 40 different purported optimizations that are all actually neutral duds, one of them will seem like a speedup and one of them will seem like a slowdown, on average.
which is understandably a bit more loony
I don't think that is what it is saying. It is saying you would write one particular optimization (your hypothesis), and then you would run the experiment (measuring speed-up) multiple times until you see a good number.
It's fine to keep trying more optimizations and use the ones that have a genuine speedup.
Of course the real world is a lot more nuanced -- often times measuring the performance speed up involves hypothesis as well ("Does this change to the allocator improve network packet transmission performance?"), you might find that it does not, but you might run the same change on disk IO tests to see if it helps that case. That is presumably okay too if you're careful.
It's just semantics, but the point is that the article wasn't saying the same thing OP was worried about. There's nothing wrong with testing B, B', B'', etc. until you find a significant performance improvement. You just wouldn't test B several times and take the last set of data when it looks good. Almost goes without saying really.
There is, in fact, "something wrong" with this, which is what GP was pointing out. It's literally covered under "Playing with multiple comparisons" in TFA.
(Personally, to combat this, I've ignored the fancy p-values and resorted to the eyeball test of whether it very consistently produces a noticable speedup.)
"It is difficult to get a researcher to stop P hacking, when his career depends on his not stopping P hacking."
It’s not a knowledge problem. It’s a vales and incentives problem.
No doubt the system needs to change, but lots of careers benefit from cheating or unethical behavior. It doesn’t rationalize it or force a choice on anyone.
Although much of the article is basic common sense, and although I'm not a statistician, I had to seriously question the author's understanding of statistics at this point. The predetermined sample size (statistical power) is usually based on an assumption made about the effect size; if the effect size turns out to be much larger than you assumed, then a smaller sample size can be statistically sound.
Clinical trials very frequently do exactly this -- stop before they reach a predetermined sample size -- by design, once certain pre-defined thresholds have been passed. Other than not having to spend extra time and effort, the reasons are at least twofold: first, significant early evidence of futility means you no longer have to waste patients' time; second, early evidence of utility means you can move an effective treatment into practice that much sooner.
A classic example of this was with clinical trials evaluating the effect of circumcision on susceptibility to HIV infection; two separate trials were stopped early when interim analyses showed massive benefits of circumcision [0, 1].
In experimental studies, early evidence of efficacy doesn't mean you stop there, report your results, and go home; the typical approach, if the experiment is adequately powered, is to repeat it (three independent replicates is the informal gold standard).
Toss a coin 10 times comes up heads 10 times. There is a 1 in 2^10 (approx 1000) that happens by chance for an unbiased coin.
I'm convinced it is biased.
20 times I am freaking convinced.
I don't need another 1000 tosses.
The author is absolutely correct. Early stopping is a classic form of p hacking. See attached image for an illustration.
If you want to be rigorous, you can define criterion for early stopping such that it's not, but you require relatively stronger evidence.
Clinical trials that stop early do so typically at predefined times with higher significance thresholds.
You will end up with much higher number of trials required to hit the P value than the version with predetermined number of trials and no stopping point by P.
Say, in a single variable single run ABX test, 8 is the usual number needed according to Fischer frequentist approach. If you do multiple comparison to hit 0.05 you need I believe 21 trials instead. (Don't quote me on that, compute your own Bayesian beta prior probability.)
The number of trials to differentiate from a fair coin is the typical comparison prior, giving a beta distribution. You're trying to set up a ratio between the two of them, one fitted to your data, the other null.
In ‘data peeking’, the flaw is that if an assay is repeated often enough, one will eventually get a result that deviates far from the mean result. This is a natural consequence of the data having a normal distribution, i.e. not all results will be identical. It's the equivalent of getting six heads or tails in a row (which should happen at least once if you flip a coin 200 times), and then reporting your coin as biased.
Repeating an assay because the distribution of the data is not what you thought, or because the likely difference between means is smaller than you thought is a valid approach.
Source: Big little lies: a compendium and simulation of p-hacking strategies Angelika M. Stefan and Felix D. Schönbrodt
I think you may want to start the questioning closer to home.
Early stopping is fine as long as the test has been designed with the possibility of early stopping in mind and this possibility has been factored in the p - value formulation.
Somebody would say “here’s an old dataset that didn’t work out, I bet you can use one of those new stats methods you’re always reading about to find a cool effect!”, and then the fishing expedition takes off.
A couple weeks later you show off some cool effects that your new cutting edge results were able to extract from an old, useless dataset.
But instead of saying “that’s good pilot data, let’s see if it holds up with a new experiment”, you’re told “you can publish that! Keep this up and maybe you’ll be lucky enough to get a job someday!”
Normally when doing that you need a multiple comparison corrections and conservative stats. That won't get you published though, or if you do get published you won't get noticed except by someone running a meta analysis. Perhaps not even then. Usually you end up with negative results from reanalysis, evidence of tampering or small effect sizes.
And this does not that reliably detect dataset manipulation, p hacking on the part of experimenters or accidental violations of the protocol, not even necessarily if the data collection included measures to prevent it.
In short: you cannot 100% trust any dataset you did not make. Not even as part of the team that makes it.
Where this gets dangerous is when it is taken at face value, either in scientific circles, or, more common, journalistic circles.
In be beginning it always felt obvious what hacking was or wasn't but towards the end it really felt hard to distinguish. I think that was the point. It created a lot of self doubt which led to high levels of scrutiny.
Later I worked as an engineer and saw frequent examples of errors you describe. One time another engineer asked if we could extrapolate data in a certain way, I said no and would likely lead to catastrophic failure. Lead engineer said I was being a perfectionist. Well, the rocket engine exploded during the second test fire, costing the company millions and years of work. The perfectionist label never stopped despite several instances (not to that scale). Any extra time and money to satisfy my "perfectionism" was greatly offset by preventable failures.
Later I went to grad school for CS and it doesn't feel much different. Academia, big tech, small tech, whatever. People think you plug data into algorithms and the result you get is all there is. But honestly, that's where the real work starts.
Algorithms aren't oracles and you need to deeply study them to understand their limits and flaws. If you don't, you get burned. But worse, often the flame is invisible. A lot of time and money is wasted trying to treat those fires and it's frequent for people to believe the only flames that exist are the obvious and highly visible ones.
These are topics you can generally learn on your own (maybe why no consolidated class?). The real key is to ask a bunch of questions about your metrics. Remember: all metrics are guides, as they aren't perfectly aligned with the thing you actually want to measure. You need to understand the divergence to understand when it works and when it doesn't. This can be tricky, but to get into the habit constantly ask yourself "what is assumed". There are always a lot of assumptions. Definitely not something usually not communicated well...
Huh. I’m not on a university connection or anything. Is it just open access?
> Running experiments until you get a hit
But if I'm running an experiment how do I know how many time to run it.
Small effect with high confidence => more samples
Big effect with low confidence=> less samples
~Ernest Rutherford.
~Psychologists
>What are statistics?
~Computer scientists
My theory isn't that Psychologists are bad at statistics. It's that the remaining problems involve lots of messy interactions and messy data that all but require statistical techniques. We just don't have the tools to extract obvious causality amidst such complexity.
I’m not criticizing the article, rather bemoaning the fact that it’s needed. Of course the problem is not just with the much maligned social sciences, it’s physics and computer science too. The controversy around Microsoft’s topological qubits, a super complex topic, in part involved the most basic kind of this nonsense, something like including 4 samples of 20 measured in the paper iirc.
The community needs to get its shit together. The world we’re living in now, the post truth era, is the result of many factors but this is one of them. The loss of faith in science is partially a self-inflicted wound.
And it has to have teeth -- withdrawn studies have to have a reputational risk that affects the credibility of future studies, even if it means publishing a retrospective or a null result in a minor journal.
And you could mitigate that risk by publishing research that doesn’t really matter, so no one ever checks.
A classic one is looking at eg an eeg topographic plot, notice which areas or channels within an area seem to be more promising, and running stats and follow ups on these. There are of course degrees of these: people may have preregistered which area (let's say prefrontal cortex for example) but leave open which channels (because it is a bit hard to make that exact guesses anyway). There are methods to deal with this (eg cluster permutation analysis) but often people seem to think that they have to choose between averaging between too many channels, thus risking smoothening out and decreasing an existing effect, or cherry-picking channels based on visual inspection of the data, which means artificially increasing an existing effect or even creating an artifactual one. Because people do not actually run a test to pick the channels, they just visually inspect the data, they do not actually realise this is p-hacking. The problem is that determining the researcher's degrees of freedom is not an easy task, and not one that can just be formalised in a p-adjustment technique.
There is a huge spectrum of practices around these degrees of freedom, that may happen during any stage of the data processing, that range from obviously to subtly sketchy and problematic. And believe me that often people who do that think that they actually have good practices, and others do p-hacking.
Imo the main way to actually avoid this issue is actually being transparent with all the decisions one makes, even if this can reduce the faith on one's results (which actually should be the point of it, if that's the case!). A lot of time shit happens, and often it is hard to predict everything in advance in a preregistration. If the incentive was to just play safe then not much innovation and method experimentation would occur. It is easy to talk about preregistration as panacea in fields with long ago established practices, but much harder when the state of the art wrt both methods and theory may change wildly even in 2 years that may take to run a study.
I believe we need better frameworks for rigorous exploratory research. The only paper I have seen to actually take this idea seriously is this one [0], but I believe a lot of research would more honestly fit in such a framework, and not everything should be conceptualised within a hypothesis testing framework.
Method-wise, closed testing procedures also seem very interesting for such research (and can work both actually inferentially, but also for extracting hypotheses for further testing), such as [1].
[0] https://pmc.ncbi.nlm.nih.gov/articles/PMC7098547/
[1] https://openpharma.github.io/CTP/articles/closed_testing_pro...
p4ul•2mo ago
And moreover, I would be even more supportive if we found a way to change the incentives for tenure and promotion such that reproducibility was an important factor in how we make decisions about grants, tenure, and promotion.
analog31•2mo ago
Disclosure: I left academia before I had to worry about any of this.