I was heavily encouraged to do what would later be called “p-hacking”, but it looked different from what they describe here. This article describes p-hacks for people that aren’t into math/stats. I always ended up p hacking because I was into stats methods.
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!”
The practice you describe is called data dredging though. The thing about it is that you do not know enough experimental design details to make sure it was all on the up, especially worse the older the dataset gets.
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.
If you "dredge" any data set (even the one you can 100% trust) over and over with random hypotheses until p-value is <0.05, you will eventually (actually, pretty quickly) support some false hypothesis. That's why "data dredging" is also p-hacking.
Yes, as I understand it there is bias inherent in any dataset due to the fact it is a sample. Data dredging is just looking for that bias. You could do that, but then you'd have to confirm with a new experiment.
The bias towards positive hypotheses is a consequence of the lack of fundamental discoveries. Most scientific researchers at this point are publicly funded engineering projects with no expected ROI. This is not a bad thing per se, but the culture of research based around making an impression in some noble's court is no longer viable. The incentives need to be shifted to good research and good methodology and need to be results agnostic.
As long as there is transparency about the process, I think this sort of thing is basically fine. It's roughly at the level of observational science rather than experimental science, and it can help lead to new research to validate the effect discovered.
Where this gets dangerous is when it is taken at face value, either in scientific circles, or, more common, journalistic circles.
> Stopping an experiment once you find a significant effect but before you reach your predetermined sample size is classic P hacking.
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).
> I had to seriously question the author's understanding of statistics at this point.
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.
There are of course statistical methods designed to support early stopping. But I don’t think you can use a regular p-test every day and decide to stop if p < 0.05. That’s something else.
You use full both sided ANOVA F test with multiple comparison correction for that. Even these tests are sometimes not conservative enough, because the correction is a bit of a guess.
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.
Multiple comparisons and sequential hypothesis testing / early stopping aren't the same problem. There might be a way to wrangle an F test into a sequential hypothesis testing approach, but it's not obvious (to me anyway) how one would do so. In multiple comparisons each additional comparison introduces a new group with independent data; in sequential hypothesis testing each successive test adds a small amount of additional data to each group so all results are conditional. Could you elaborate or provide a link?
In lots of human studies, you can’t just stop at an arbitrary number of participants because you’ve counterbalanced manipulations to decorrelate potential confounders (e.g., which color stimulus is paired with reward, the order of trials).
The distinction is between ‘data peeking’, i.e. repeatedly checking the p-value you've obtained and stopping if it falls below 0.05, and repeating assays in the light of new information. Such new information can relate to the distribution of the values, the expected effect size, or any other parameter that you did not know at the outset of the study.
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
Sounds like a variable cost experiment. Each observation cost x$. Like an A/B split on Google ads. Why keep paying for A when you know B is better already.
It’s more like you are supposed to toss 1000 times and after 500 tosses you get a lucky streak of 5 heads in a row and then decide to end experiment and conclude that coin is biased.
Google Optimize used to tell you to let an experiment run for one-two weeks (?), exactly because early strong results tend to not don't hold up in the long run.
I don't know, maybe knowing when to "hold them" versus "fold them" and "walk away" would be a valuable skill here. The phrasing sounds off in the part you quite because in poker you only can play a given hand once, and after you've lost, you need to draw an entirely new dataset and start fresh.
It is an old saying, and I’m not sure there’s much use to it as it feels like a mitigation.
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.
The Bonferroni correction part of this article is the most important. The amount of papers that don't account for this is shocking, comparing 20 variables with a 0.05 confidence interval is extremely annoying, as you end up having to do analysis on all papers data yourself to correct for it to see if it is still significant or not.
If the conclusion is "be transparent", I'm strongly supportive.
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.
Won’t these just make it less likely that you can publish your work, and end up damaging your career in the short term? As opposed to getting published, having a career, with a long tail risk of being found out later?
And you could mitigate that risk by publishing research that doesn’t really matter, so no one ever checks.
It's not that they suck at statistics. It's that their statistics and experimental designs are artificially stuck in the dark ages. This is forced on the world by the academic publishing industry - you publish this way, or you perish. The completely unsurprising result is a reproducibility crisis that undermines the entire field. Check out "Bernoulli's Fallacy" for a good overview.
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.
Not really - it just shows up so much in psychology because they need statistics much more than, say, physics. Most physics programs in the US do not even teach statistics as a subject.
The article cuts off for me so I do not know if they talk about this, but preregistration has to be part of the conversation moving forward.
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.
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.
> 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.
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.
"Multiple times" doesn't have to mean "no modifications". Suppose the software is currently on version A. You think that changing it to a version B might make it more performant, so you implement and profile it. You find no difference, so you figure that your B implementation isn't good enough, and write a slight variation B', perhaps moving around some loops or function calls. If that makes no difference, you keep writing variations B'', B''', B'''', etc., until one of them finally comes out faster than version A. You finally declare that version B (when properly implemented) is better than version A, when you've really just tried a lot more samples.
Well it does mean "no modifications" to the hypothesis, hypothesis being about performance of code A and B. Code B' would be a change.
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.
Sure, it may not be precise repetition, but my idea here is that none of B', B'', etc. are really different than B (they may even compile down to the exact same bytecode), they're just the same thing but written differently. And in fact, none of these are really faster than A, even if they're all "changes". But it's the same issue as any other form of p-hacking, where you keep trying more and more trivial B-variations until you eventually get the result that you're looking for, by random chance. (Cf. the example in xkcd 882, which does change the experimental protocol each time, but only trivially.)
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.)
Perf, though? If a perf optimization changes the UI noticeably other than by making it smoother or otherwise less janky, someone is lying to someone about what "performance" means. Likely though that be, we needn't embarrass ourselves by following the sad example.
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.
I thought languages such as Rust and flamegraphs and etc were supposed to help us avoid doing all this testing and optimization right? Like I use the built in analysis tools that come with cargo and such and what I have on my os, tools like cutter or reverse engineering tools. Even on python I use the default or standard profiling and optimization tools, I wonder sometimes if I am not doing something enough if the default tools thats recommended should cover most edge cases and performance cases right?
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.
Well, what is the test you are using to measure performance? Maybe the optimizations help performance in some cases and hurts performance in others... your test might not fully match all real world workloads.
These seem like two different things. Testing many different optimizations is not the same experiment; it's many different experiments. The SE equivalent of the practice being described would be repeatedly benchmarking code without making any changes and reporting results only from the favorable runs.
Doesn’t matter if it’s the same experiment or not.
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.
That's not p hacking. That's just the nature of p values. P hacking is when you do things to make a particular experiment more likely to show as a success.
There's another cheeky example of this where you select a pseudo-random seed that makes your result significant. I have a personal seed, I use it in every piece of research that uses random number generation. It keeps me honest!
what they’re referring to might be better put as applying a patch once and then running it 500 times until you get a benchmark thats better than baseline for some reason
It might be below the fold, but it looks like they're missing the most important p-hacking strategy of all: the dogshit null hypothesis. It's very reliable and it's the most common type of p-hacking that I see.
It'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.
If I understand the parent commenter, here's a common example from population-level statistics like public health:
"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.
"I ran a t-test on the untreated / treated samples and the difference is significant! The treatment worked!"
...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.
I think you're more observing an issue with experimental models not challenging a null hypothesis, than with poor null hypotheses themselves. In other words, papers creating experiments that don't actually challenge the hypothesis. There was a major example of this with COVID. A typical way observational studies assessed the efficacy of the vaccines was by looking at outcomes between normalized samples of nonvaccinated and vaccinated individuals who came to the hospital and seeing their overall outcomes. Unvaccinated individuals generally had worse outcomes, so therefore the vaccines must be effective.
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.
Null hypotheses are often idealized distributions that are mathematically convenient and are often over-simplifications of the distributions we'd expect if there were truly no effect (because the expected distributions are either intractable to work with, or irregular and unknown).
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.
Reading this article tbh causes second hand embarrassment. Ostensibly it’s targeting professional scientists using the brand of a prestigious journal, yet it has a vibe of explaining ethics and common sense to school kids. We’ve come to the point of having to explain to PhDs why cherry picking data is bad.
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.
Before you start your experiment, you calculate how many samples you need based on the estimated effect size you're looking for and how small you want your confidence interval to be.
In the physical sciences you can often estimate the noise level in a null measurement -- or even measure it. You often do this just to get your setup working before doing something like wasting a precious specimen on a "this time for real" measurement.
> 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.
> 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.
There are many more or less obvious ways that people do p-hacking without even realising it.
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].
I was heavily encouraged to do what would later be called “p-hacking”, but it looked different from what they describe here. This article describes p-hacks for people that aren’t into math/stats. I always ended up p hacking because I was into stats methods.
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!”
The practice you describe is called data dredging though. The thing about it is that you do not know enough experimental design details to make sure it was all on the up, especially worse the older the dataset gets.
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.
If you "dredge" any data set (even the one you can 100% trust) over and over with random hypotheses until p-value is <0.05, you will eventually (actually, pretty quickly) support some false hypothesis. That's why "data dredging" is also p-hacking.
Yes, as I understand it there is bias inherent in any dataset due to the fact it is a sample. Data dredging is just looking for that bias. You could do that, but then you'd have to confirm with a new experiment.
The bias towards positive hypotheses is a consequence of the lack of fundamental discoveries. Most scientific researchers at this point are publicly funded engineering projects with no expected ROI. This is not a bad thing per se, but the culture of research based around making an impression in some noble's court is no longer viable. The incentives need to be shifted to good research and good methodology and need to be results agnostic.
As long as there is transparency about the process, I think this sort of thing is basically fine. It's roughly at the level of observational science rather than experimental science, and it can help lead to new research to validate the effect discovered.
Where this gets dangerous is when it is taken at face value, either in scientific circles, or, more common, journalistic circles.
> Stopping an experiment once you find a significant effect but before you reach your predetermined sample size is classic P hacking.
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).
[0]: https://pubmed.ncbi.nlm.nih.gov/17321310/
[1]: https://pubmed.ncbi.nlm.nih.gov/16231970/
No, it's generally not valid -- it will depend on the specifics of the test (especially if the test is valid only asymptotically). You need some method that supports sequential inference. Nowadays your best bet is probably some sort of anytime-valid method from the e-value literature https://en.wikipedia.org/wiki/E-values https://projecteuclid.org/journals/statistical-science/volum...
> I had to seriously question the author's understanding of statistics at this point.
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.
There are of course statistical methods designed to support early stopping. But I don’t think you can use a regular p-test every day and decide to stop if p < 0.05. That’s something else.
You use full both sided ANOVA F test with multiple comparison correction for that. Even these tests are sometimes not conservative enough, because the correction is a bit of a guess.
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.
Multiple comparisons and sequential hypothesis testing / early stopping aren't the same problem. There might be a way to wrangle an F test into a sequential hypothesis testing approach, but it's not obvious (to me anyway) how one would do so. In multiple comparisons each additional comparison introduces a new group with independent data; in sequential hypothesis testing each successive test adds a small amount of additional data to each group so all results are conditional. Could you elaborate or provide a link?
The general topic and some specific ways to estimate a correction are described under this term: https://en.wikipedia.org/wiki/Sequential_analysis
In lots of human studies, you can’t just stop at an arbitrary number of participants because you’ve counterbalanced manipulations to decorrelate potential confounders (e.g., which color stimulus is paired with reward, the order of trials).
The distinction is between ‘data peeking’, i.e. repeatedly checking the p-value you've obtained and stopping if it falls below 0.05, and repeating assays in the light of new information. Such new information can relate to the distribution of the values, the expected effect size, or any other parameter that you did not know at the outset of the study.
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
https://royalsocietypublishing.org/doi/10.1098/rsos.220346
https://commons.m.wikimedia.org/wiki/File:P-hacking_by_early...
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.
The region where `p` hits the red line should be called "publish or perish".
Sounds like a variable cost experiment. Each observation cost x$. Like an A/B split on Google ads. Why keep paying for A when you know B is better already.
Small samples have more variability than large samples and thus more often show spurious large effects.
So you end up with a higher threshold for confidence at p<0.05 ot whatever you want p to be under. Comes out in the maths!
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.
It’s more like you are supposed to toss 1000 times and after 500 tosses you get a lucky streak of 5 heads in a row and then decide to end experiment and conclude that coin is biased.
Google Optimize used to tell you to let an experiment run for one-two weeks (?), exactly because early strong results tend to not don't hold up in the long run.
-> https://en.wikipedia.org/wiki/Regression_toward_the_mean
Seasonality effects, too
There is another reason to keep clinical trials as long as designed. To understand the safety and side effects implications.
> As any gambler knows, if you roll the dice often enough, eventually you’ll get the result you want by chance alone
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.
Nicely done. Since many folks may not know the original song: https://en.m.wikipedia.org/wiki/The_Gambler_(song)
(And TIL, this wasn't original to Kenny Rogers!)
I almost did this verbatim quote of the lyrics, which paralleled the article's sentence, and is relevant to P-hacking, but it's the wrong advice:
I don't know, maybe knowing when to "hold them" versus "fold them" and "walk away" would be a valuable skill here. The phrasing sounds off in the part you quite because in poker you only can play a given hand once, and after you've lost, you need to draw an entirely new dataset and start fresh.
Like the old saying goes,
"It is difficult to get a researcher to stop P hacking, when his career depends on his not stopping P hacking."
It is an old saying, and I’m not sure there’s much use to it as it feels like a mitigation.
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.
Yeah that was kind of my feeling too while skimming through this: ”Good luck with that…”
It’s not a knowledge problem. It’s a vales and incentives problem.
The Bonferroni correction part of this article is the most important. The amount of papers that don't account for this is shocking, comparing 20 variables with a 0.05 confidence interval is extremely annoying, as you end up having to do analysis on all papers data yourself to correct for it to see if it is still significant or not.
If the conclusion is "be transparent", I'm strongly supportive.
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.
Just make it even more cutthroat than it already is. Replacing one hackable incentive system with another will just produce a new set of hacks.
Disclosure: I left academia before I had to worry about any of this.
Won’t these just make it less likely that you can publish your work, and end up damaging your career in the short term? As opposed to getting published, having a career, with a long tail risk of being found out later?
And you could mitigate that risk by publishing research that doesn’t really matter, so no one ever checks.
>If you need statistics, you did the wrong experiment.
~Ernest Rutherford.
>If you don't need statistics, you did the wrong experiment.
~Psychologists
>What are statistics?
~Computer scientists
Psychologists are notoriously bad at statistics though
It's not that they suck at statistics. It's that their statistics and experimental designs are artificially stuck in the dark ages. This is forced on the world by the academic publishing industry - you publish this way, or you perish. The completely unsurprising result is a reproducibility crisis that undermines the entire field. Check out "Bernoulli's Fallacy" for a good overview.
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.
Not really - it just shows up so much in psychology because they need statistics much more than, say, physics. Most physics programs in the US do not even teach statistics as a subject.
The irony of the article appearing in the "career" section when following its advice means you'll not have a career
The article cuts off for me so I do not know if they talk about this, but preregistration has to be part of the conversation moving forward.
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.
The worst part about this:
> 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.
> 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.
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.
"Multiple times" doesn't have to mean "no modifications". Suppose the software is currently on version A. You think that changing it to a version B might make it more performant, so you implement and profile it. You find no difference, so you figure that your B implementation isn't good enough, and write a slight variation B', perhaps moving around some loops or function calls. If that makes no difference, you keep writing variations B'', B''', B'''', etc., until one of them finally comes out faster than version A. You finally declare that version B (when properly implemented) is better than version A, when you've really just tried a lot more samples.
Well it does mean "no modifications" to the hypothesis, hypothesis being about performance of code A and B. Code B' would be a change.
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.
Sure, it may not be precise repetition, but my idea here is that none of B', B'', etc. are really different than B (they may even compile down to the exact same bytecode), they're just the same thing but written differently. And in fact, none of these are really faster than A, even if they're all "changes". But it's the same issue as any other form of p-hacking, where you keep trying more and more trivial B-variations until you eventually get the result that you're looking for, by random chance. (Cf. the example in xkcd 882, which does change the experimental protocol each time, but only trivially.)
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.)
Why is this bad for you? You're optimizing software, not trying to describe reality. Monte Carlo and Drunkard's Walk are fine.
You're churning the user experience for no reason. Maybe constant optimization churn is one of the reasons why UIs are so bad.
Perf, though? If a perf optimization changes the UI noticeably other than by making it smoother or otherwise less janky, someone is lying to someone about what "performance" means. Likely though that be, we needn't embarrass ourselves by following the sad example.
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.
I thought languages such as Rust and flamegraphs and etc were supposed to help us avoid doing all this testing and optimization right? Like I use the built in analysis tools that come with cargo and such and what I have on my os, tools like cutter or reverse engineering tools. Even on python I use the default or standard profiling and optimization tools, I wonder sometimes if I am not doing something enough if the default tools thats recommended should cover most edge cases and performance cases right?
Yeah!
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
heck even the ai by default doesnt start with security from the models I have tested its really really weird.
Well, what is the test you are using to measure performance? Maybe the optimizations help performance in some cases and hurts performance in others... your test might not fully match all real world workloads.
These seem like two different things. Testing many different optimizations is not the same experiment; it's many different experiments. The SE equivalent of the practice being described would be repeatedly benchmarking code without making any changes and reporting results only from the favorable runs.
Doesn’t matter if it’s the same experiment or not.
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.
That's not p hacking. That's just the nature of p values. P hacking is when you do things to make a particular experiment more likely to show as a success.
There's another cheeky example of this where you select a pseudo-random seed that makes your result significant. I have a personal seed, I use it in every piece of research that uses random number generation. It keeps me honest!
what they’re referring to might be better put as applying a patch once and then running it 500 times until you get a benchmark thats better than baseline for some reason
which is understandably a bit more loony
Nah it could be 20 different patches.
how can I do this in python what modules?
This is one of the most disturbing articles I have seen related to reproducibility because it seems to imply that scientists don’t already know this.
As a biologist all the field wants is p < 0.05. What it actually means is unnecessary. It's a hurdle to pass to have another paper on your CV.
It might be below the fold, but it looks like they're missing the most important p-hacking strategy of all: the dogshit null hypothesis. It's very reliable and it's the most common type of p-hacking that I see.
It'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.
This would be much better with an example
If I understand the parent commenter, here's a common example from population-level statistics like public health:
"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.
"I ran a t-test on the untreated / treated samples and the difference is significant! The treatment worked!"
...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.
I think you're more observing an issue with experimental models not challenging a null hypothesis, than with poor null hypotheses themselves. In other words, papers creating experiments that don't actually challenge the hypothesis. There was a major example of this with COVID. A typical way observational studies assessed the efficacy of the vaccines was by looking at outcomes between normalized samples of nonvaccinated and vaccinated individuals who came to the hospital and seeing their overall outcomes. Unvaccinated individuals generally had worse outcomes, so therefore the vaccines must be effective.
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.
> looks like they're missing the most important p-hacking strategy of all: the dogshit null hypothesis
Would you mind giving an example(s) of such and how it differs from a "good" null hypothesis?
Null hypotheses are often idealized distributions that are mathematically convenient and are often over-simplifications of the distributions we'd expect if there were truly no effect (because the expected distributions are either intractable to work with, or irregular and unknown).
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.
Reading this article tbh causes second hand embarrassment. Ostensibly it’s targeting professional scientists using the brand of a prestigious journal, yet it has a vibe of explaining ethics and common sense to school kids. We’ve come to the point of having to explain to PhDs why cherry picking data is bad.
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.
> Ending the experiment too early
> Running experiments until you get a hit
But if I'm running an experiment how do I know how many time to run it.
Before you start your experiment, you calculate how many samples you need based on the estimated effect size you're looking for and how small you want your confidence interval to be.
Small effect with high confidence => more samples
Big effect with low confidence=> less samples
In the physical sciences you can often estimate the noise level in a null measurement -- or even measure it. You often do this just to get your setup working before doing something like wasting a precious specimen on a "this time for real" measurement.
> You have full access to this article via your institution.
Huh. I’m not on a university connection or anything. Is it just open access?
Non-paywall link: https://archive.is/IJcOI
see also: Andrew Gelman's blog
> 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/...
There are many more or less obvious ways that people do p-hacking without even realising it.
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...
Imagine if Nature simply didn't publish obviously p-hacked papers. Perhaps that would do more than a blog post.