>Researchers should embrace negative results instead of accentuating the positive
The problem starts here. Most researchers would love to show their negative results, they're well aware of the problem. But they need to publish, they need grants, they need money which is outcome independent. They need an alternative reality where negative results and reproducibility studies make money.
As it stands you get money for publishing praise, a lot of industrially sponsored medical research is just "9/10 doctors recommend x" advertising.
We need to instate the rule that only preregistered studies can be published or at least used by the FDA as for decisions.
Right now you can conduct 1000 studies until you find a handful which randomly show the result you want.
> The problem starts here. Most researchers would love to show their negative results
There's another core issue which most people miss. In science, you need to publish results AND explain WHY. That last part of WHY is crucial. The amount of work required to prove a negative - or explaining WHY - is very very high and in many cases close to impossible.
Typically studies do not report negative but lack of null hypothesis rejection (means "we do not know if it does anything"). What we also need is effect sizes (risk reduction, number needed to treat). When a study significantly shows tiny effect size, it is much more damning.
Like all human systems, you get what you optimize for.
Universities want paid grants for money and prestige, so the that's what the researchers go find. I've said this before on here but the solution to this problem is the universities like Harvard and foundations like RWJ which have near infinite money and don't need to operate like this. They need to push forward real research that is reproducible (maybe several times) and shows whatever the data really shows. The researchers who create reproducible studies get bonuses. Again, you get what you optimize for.
The number of discussions I have had with the staff in mathematics and computer science about the
need for such journals would last years. Everyone pretty much wants them because they know the need
of saying "hey I already did this and we got nowhere - try something else" is so crucial for science and mathematics.
> We need to instate the rule that only preregistered studies can be published or at least used by the FDA as for decisions.
That won't help, not by itself. Preregistration helps with "p hacking", the practice of moving the goal posts until some result become significant. A bigger problem remains.
Medicine and Biology accepted the framework of Statistical Hypothesis Inference Testing, where a null hypothesis is rejected at some p-value, usually 0.05. Ignoring many faults of this framework (for example that the alternative hypothesis is not tested at all, that it is a bad caricature of the bad statistics R. A. Fisher introduced, that the numerical outcomes depend on the probability of events that didn't happen, etc.), the logic is that you limit the false positive rate to below the p-value threshold.
Unfortunately, journals consistently reject submission, unless there is a significant p-value somewhere in there. ("Highly significant" is better, even though the term makes no sense.) So if plenty of researchers investigate some random nonsense where the null hypothesis is actually true, 100% of published studies will be spurious results, preregistration or not.
To make progress, this kind of statistics has to go. Journals would have to change their policies, which probably means peer reviewers have to change theirs. I have no idea how to make that happen.
Preregistration does help with this issue a bit. It won't make published studies any better, but it still helps solve the file-drawer problem if the results are available somewhere. If you take a shotgun approach to getting significance out of null hypotheses, you presumably get 5% successes. (Sort of. Maybe. p-values really stink, as you point out.) But if 20 people all run variants of the same bunk study, preregistration means that instead of just seeing one success, we see one success on the cover of PNAS, and then at least have the option to look up the ~10 prior failures and decide not to accept the conclusion. (Well, one time in twenty it'll be the first try, but it's still progress.)
Of course, that's still going to push researchers to change up their techniques for getting false positives. It rewards either covering unexplored domains (so there's no counterexample to your false positive), or exploiting other tricks to manipulate significance in preregistered work.
I don't think existing journals have much hope of improving their practices, honestly. Between their ludicrous financial incentives and ideologues talking "methodological terrorism", that matter seems depressingly settled. But I wonder if there might be hope for creating a counterweight to this?
What happens if Gelman and Khahneman get together to create the Very Prestigious Journal of Replications and the Somewhat Prestigious Journal of Rejected Hypotheses? The first one is neat because it rewards negative results, since they change the state of what's understood - at the very least it might encourage more people to start checking the most influential and most suspicious results. The second thing might be a harder sell, but it could reward comprehensive negative work on key topics (much like Alzheimer's research has heavily consisted of excluding possible pathways). Honestly, "create new prestigious journals from scratch" sounds far easier than "reform existing journals" or "tenure and reward professors for reasons other than publications".
> Honestly, "create new prestigious journals from scratch" sounds far easier...
What used to be "prestigious" has come to mean "high impact factor", mostly because funding agencies needed an "objective" way to grant funding, and being run by bureaucrats, they picked impact factor as a measure of scientific success. For a Journal Of Replications to have impact, researchers would have to cite papers about replications. But that's not expected; you cite the original paper, not the one that replicates a result, and you never hear about the one that failed to reproduce a result.
I don't see that approach working, but I'd like to see someone try it.
> For a Journal Of Replications to have impact, researchers would have to cite papers about replications.
Yep, this is definitely the biggest weakness for the idea. A journal about replications would probably end up with low impact factor, and wouldn't be able to grab a groundbreaking result to boost its prestige the way some narrow-topic journals have.
My only thought for handling that was alluded to with "Gelman and Kahneman"; maintaining a tolerable reputation and impact factor would probably require leaning on big names and people who are devoted to doing replication work regardless of journal. Gelman, for instance, showed up in PNAS with references when he criticized that godawful "boarding and air rage" study. If we're willing to abuse the process even further, there might be room to publish methodology-of-replication papers in statistical or procedural journals and create further citations that way.
It's not a very good answer, and I don't think it's going to free anyone from "publish or perish". The best I can really hope for is creating a bit of space for talented, skeptical researchers to add replications to their other work without needing to be tenured and entrenched first.
A big part of the problem is there are too many PhDs chasing too little funding. There's no room for negative results when the competition is that big.
I wish I could find it, but there's a superb piece out there about the inherent dysfunction of lottery-style careers. The basic idea was that there are a handful of careers where success is highly rewarded, but job count and quality don't really respond to the market.
In academia, there are however many tenured professorships with whatever salary, set by largely non-market forces. In Hollywood, there are only so many recognizable stars at a time who can guarantee sales, so their salaries don't really decline no matter how many people vie for their spots. And the same in pro spots, music, politics, Harvard admissions, etc.
And the result is that without adding new jobs or dropping salaries, the people hiring balance the market somehow. Unpaid internships, selling expensive credentials, would-be singers selling hits to existing stars, massive university donations by parents, vicious hazing on football teams, horrifying abuse by casting agents; people who control these 1,000:1 (or higher) seeker-to-slot fields manage to exploit that eagerness to all kinds of horrible ends. [1]
Academia is probably less bad than many of those fields, perhaps because the rewards at the top are less spectacular. But it's not a coincidence that Brian Wansink's big scandal was about pressuring a grad student to find results in null data, or that grad students and postdocs end up working miserable hours to be third author on their own research.
I don't have an answer here, really. But I certainly agree that as long as there are endless ranks of people struggling to make their names, people are going to keep finding ways to get dramatic-looking results, data be damned.
[1] I suspect this stuff really kicks in at several hundred to one or higher. Harvard doesn't reject this percentage, but note that it applies a time-and-money filter before the applications even arrive.
I still think that science should be automated in some way, shape or form. I'm imagining something like you have a dataset and you have to upload that dataset to some third party that checks it for it's validity. Then you write exactly WHAT you are going to do with the data and then you send the proposed "routines" in, this should give automated generated output and an automated report of what was done and why. Of course, this is a completely silly idea but I'd love to know if someone has like any tangential related thoughts on this
> I still think that science should be automated in some way, shape or form.
Meaning what?
> I'm imagining something like you have a dataset and you have to upload that dataset to some third party that checks it for it's validity.
The results are what they are. What is 'validity' meant to mean?
> Of course, this is a completely silly idea but I'd love to know if someone has like any tangential related thoughts on this
Quantitative studies are already published with the proper analyses, which are invariably produced 'automatically' using software, not manual methods.
I imagine there might be some value in publishing raw data, though. There may sometimes be questions like privacy, but I don't imagine they'll always be show-stoppers.
> Then you write exactly WHAT you are going to do with the data and then you send the proposed "routines"
this roughly matches up with the idea of "preregistration" of research, i.e. you define and share what your experimental method is going to be before you start looking at the data and performing analysis, to help guard against some unconscious or conscious decisions to adjust the method after you have observed the experimental data.
i've never heard of cos.io before but they're a top hit for me when searching for "preregistration" https://cos.io/prereg/
I quite like how Gelman theoretically frames this in his "forking paths" paper:
Consider the following testing procedures:
1. Simple classical test based on a unique test
statistic, T, which when applied to the observed
data [ y ] yields T(y).
2. Classical test pre-chosen from a set of
possible tests: thus, T(y; phi), with
preregistered phi. For example, phi might
correspond to choices of control variables in a
regression, transformations, and data coding and
excluding rules, as well as the decision of
which main effect or interaction to focus on.
3. Researcher degrees of freedom without fishing:
computing a single test based on the data, but in
an environment where a different test would have
been performed given different data; thus
T(y; phi(y)), where the function phi(.) is
observed in the observed case.
4. "Fishing": computing T(y;phi_j) for j=1,...,J:
that is, performing J tests and then reporting
the best results given the data, thus
T(y; phi^{best}(y)).
My research area has actually started doing that. Sure it's a CS discipline, but yeah we have a second component of our conferences where we automate our benchmarks, and other people run those benchmarks and validate the results.
For CS publications, it should be the norm to insist on inclusion of all source-code and data-sets used, unless there's a compelling reason they can't be included.
It's absurd that reproducing results be any more of a challenge than simply re-running a freely-available program.
All but one program I wrote for scientific publications have been on the payroll of corporate grants, and the IP rights hooked right back into the company paying for the whole show. Can't exactly open-source things you don't actually own.
Then you should be denied the opportunity to publish. Corporate obstinacy should not trump good science.
Software is unique in that it can be generally be duplicated and executed trivially.
There's no way to make it trivial to reproduce a test on the strength properties of a new ceramic. There is a way to do this for software, and it's rather silly that it isn't standard scientific practice to do so.
I realise I'm taking a strong line here, but I've never seen a good argument against it.
The unfortunate answer is that instead of harder-to-reproduce science, no science would have been published in all of those cases. Quite often, sharing knowledge is a secondary goal to achieving the set goals of a project. In niche fields, input from any source is welcomed gladly, as long as the papers are sound. Banning corporate players from sharing knowledge in your journal if that's the majority source for input in the field is not really an option.
I fear that science is slowly going awry, particularly in fields where outcomes have grave and immediate implications for businesses. In this respect, physics is simpler than social science. Not getting the results you expect is fine and often teaches you something.
I don't think it's going awry but rather that certain fields have always been suspect and we're just now realizing how bad it is. In mathematics, there are proofs that have stood up for thousands of years; in physics there are models that have remained useful for hundreds. How many fields can claim that kind of longevity?
Furthermore, it would be extremely useful if scientific research was transparant from inception to outcome.
Scientific ‘papers’ are archaic forms of knowledge transfer suited for a time when physical paper was the only way. These days, science would serve us better if we could see everything involved in the process. I don’t want to see only the results, I want to see the whole notebook and all the hurdles along the way. Why can’t we follow the researchers and the accumulation of evidence in real time?
Sounds nice, but as a scientist I can say that it would be a huge overhead to have to constantly prepare half finished work for public consumption throughout the entire process of a study. Scientific papers make sense because the point is to summarize your results, discuss what they may imply, e.g what theories they support or deny, and describe what you did in a reproducible way so that the work can be verified. The writing of a paper is an act of communication. It's important that it is an explicit thing that researchers are trained to do properly, not something that they just shit out at the end of a poorly done study that didn't work, or worse, in the middle of something where they can't draw any conclusions yet. E.g. journalists already pick up on wrong or hype-inducing interpretations of poorly written press releases of published papers. Imagine if they could also pick up on half-finished work. "Study being done could mean something amazing, maybe, if it works!" You think fake news is a problem now? Imagine the world you propose.
Now, if researchers were encouraged more to describe in detail their process and everything that went right and wrong throughout a study, along with data and algorithms and everything, perhaps as appendices or in supplemental material like blogs or videos etc., and and I find this is what is happening lately, that would be fine, and a nice ideal to strive for.
But realize that scientists are already required to not only perform the study but write about it, and convince every skeptic that they are right, go to conferences and get an article accepted by a journal which can take a year or more. And now add to this that they are required to prepare the data and software for public consumption, make videos and blog posts that describe everything, answer all questions that the public has. Think about all that overhead you are demanding that goes so far above and beyond doing the actual science. It's not small. And they are not paid extra for it, in fact their paycheck is probably half what they could make doing closed science for a for-profit company. Meanwhile their job as an academic is only to explore new ideas and convince their peers of their worth. Why should they go the extra mile, for free, for every member of the public who demands answers and transparency? Sorry, but it's too. much. work.
Actually, when reading papers, I find the ‘communication’ parts to have the least value. It’s probably just me, but I try to skip over those parts because they tend to bias and frame the results. I want to understand the intent, strategy, methodology, math, models, data, outcomes, etc. but not editorializing. Plus, many good scientists aren’t necessarily experts at prose or communication, anyway. Why can’t the communication parts be provided as addendum?
For people who work in private R&D, like me, we try to keep lab notebooks so that we have records of pretty much everything imagined or tried, warts and all. Sure, it can seem haphazard, unformatted, and not packaged for general consumption. But, it’s meant for collegues anyway, and it fits the purpose.
As for your last paragraph, I totally empathize with your frustrations. But, those seem to be more structural issues with the economics and politics of science and the academies. I certainly would love to see change there, as well. I wish research could be funded in different ways. But, as a consumer of research, I can only really describe my particular use cases.
What I mean by "communication" is what you describe as "the intent, strategy, methodology, math, models, data, outcomes." What do you mean by editorializing? If you mean discussing implications on existing theories, I think this can be done badly or done well (like all parts of a paper.) But when doing research it's important to read follow-ups and rebuttals. We can't forget that science is a process, an on-going discussion. It's not a single result or paper.
I think many readers (science journalists, in particular) only read the abstract, introduction, and then immediately jump to the conclusions.
The introduction section almost always frames the paper with opinions and biases. And, the conclusion section often focuses too heavily on how great the results are (and the author’s prowess) without identifying interesting issues or irregularities encountered in the methodology, data, or outcomes.
I get that publishing is a huge part of a scientist’s career success and for self-promotion, but I see many papers that over emphasize those aspects. Again, I don’t fault them. One can’t easily get funding without a reputation. But, in my idealized (and probably unrealistic) world it would be different.
I do want to stress that I’m not complaining. What I have access to is amazing. But, sometimes I wish I could see it all.
> Sounds nice, but as a scientist I can say that it would be a huge overhead to have to constantly prepare half finished work for public consumption throughout the entire process of a study.
How about writing into a (public) blog, instead of a lab notebook?
First, my notes are not nearly well-organized enough to have any kind of coherence for anyone but me. Do you think it's interesting for me to answer public questions, to defend ideas that I haven't even completely thought through yet? But secondly, why would I want to publish my half-baked, unproven ideas? I can see two possible outcomes: (1) I completely embarrass myself because they are stupid ideas that I haven't verified, or (2) they are good ideas and someone takes them and runs faster than I can and beats me to a result. I see zero advantage for me to do what you say.
I think this idea of let's do every step of science 100% in the open are completely forgetting that science is a social process. Putting things out there has consequences. The onus is on the scientist to verify things before saying them. There is a word for "scientists" who do not. Personally I don't believe that that is something that will change in the next 100 years.
The current “science as a career” model of science with public grants etc stems entirely from the development of the atomic bomb and World War II resulting in Vanevar Bush proposal of the NSF. I sincerely doubt that science will be practiced anything like it’s current form in 100 years. What it will look like is an interesting question.
Great so people hostile to your research (eg Republicans) can turn your research
political because they can take your notes out of context (try using the word "trick" in your research journal or emails)
and use it against you or your research area.
“Why should they go the extra mile, for free, for every member of the public who demands answers and transparency? Sorry, but it’s too. much. work.“
I understand your exhaustion at the idea, truly, but in an era of publicly funded research, the public does have a right to demand transparency for the same through Congress (in America).
That said, a more reasonable level of transparency, post-facto, ought to be sufficient for for most - emails, data, etc. get requested of members of the Congress, for example. Or for a more representative example, take a look at the explanatory efforts of the Federal Reserve and when they go beyond the plain economic research to also provide detailed public transparency.
Oh I agree with you that these things should be made available if requested in a serious way. I also think scientific papers should be open access, for similar reasons. I'm not advocating keeping anything secret. And in general if someone takes the time to email me about a question regarding my work, of course I'm going to take the time to give a thorough answer to the best of my ability. But here I was responding primarily to the idea that scientists should report every bit of progress (or non-progress) in real time as it happens, and also to the statement that the scientific paper is an out-dated concept, which I happen to disagree with.
Yeah, that idea that you are responding to is the daily reality for a lot of software professionals. Especially if you replace the noun “public” with the noun “management”.
A growing number of people seem to agree with this ([0],[1]). There are a couple of places ([2],[3]) where one can preregister a hypothesis and experiment before collecting data. There are also some journals that are starting to encourage preregistration ([4],[5]). It would be nice if this phenomenon spread beyond the few fields it's started in.
I don't know about needing to see all the intermediate data, that seems extreme if the methodology is properly described and the raw data is available.
> preregister a hypothesis and experiment before collecting data
This reminds me of an old website, I think it was called Half Baked, where people could (I think anonymously) post just any ridiculous idea for an invention. It was fun to read. Unfortunately I can't find a link.
But man, when I think about it in terms of science and in the more modern context of preprints, it sounds like Flag Planting, Extreme Edition. Even the ML community, who encourage preprint publication more than any other field I know of, have had some pretty heated exchanges about the validity of using that medium for flag planting, and that is when the "flag planting" at least consists of a short paper properly describing an idea, with some rudimentary empirical result and analysis.
So I dunno, it's an intriguing idea, but not without controversy I think.
I got put off science at high school when I'd get marked down for having "wrong" but truthful results to physical experiments, so I ended up going around and averaging out other people's results (not their conclusions or write-ups, just the raw numerical measurements) which yielded better marks. I wonder if an element of that is at play in corners of the broader scientific community.
High school physics experiments are somewhat of a different case, as "wrong but truthful" results are probably evidence of an incorrectly performed experiment, performing which correctly is part of what one is assessed on. That, or bad luck, but presumably the experiments are sufficiently simple that performed correctly they all but guarantee a "correct" result.
i guess it depends how complex the experiments are at your particular high school, but in my experience we did not have terribly precise instruments or techniques, so the labs would have a high degree of random error. since the lab usually had to fit into 75 minutes, the procedure usually didn't call for many trials. labs where we would perform 5 or more (up to twenty in one lab) trials for each step in college might have 3 or even just one trial in high school.
if you have poor quality equipment and very few trials, the results are going to be all over the place. if you average the whole class's values, you might actually get close.
The time I learned how important it is to forge numbers is when we were measuring gravity in high school by rolling a ball off the end of a table and using a stopwatch to time how long it took to fall to the ground by starting it when the ball fell off the end and stopping it when it hit the ground.
To free fall one meter on Earth is about .45 seconds.
If you are systematically off and get .35 seconds, you get a gravity of 16m/s^2. If you are systematically off and get .55 seconds, you get a gravity of 6.5m/s^2. It isn't that hard to be systematically off in your button presses by that amount even in ten trials. The noise is huge compared to the signal, and averaging several attempts can only smooth out random noise, not systematic miscalculations of when the ball leaves the table or lands.
I got the second result. I got a bad grade. I learned my lesson. Remarkably every subsequent experiment I ever ran was within ten percent of the real value. My turnaround was truly amazing.
The problem with "studies/research" today is that most of it cannot reproduced, not that it went nowhere. It's not really a matter of "cleaning up" the research to make it "positive". In other words, most science today isn't real science.
Throw in the issues of funding ( government - political issues, private - corporate issues ) and there is very little incentive for real research. And with the current academic environment at leading institutions like Yale, scientists probably are too afraid to do research honestly on sensitive topics.
Also, isn't this just a rehash of another nytimes article from last year?
There are 3 or 4 nytimes articles on the frontpage. At this rate, how long before the entire frontpage is just nytimes? Just redirect hn to nytimes and be done with it?
The NY Times just rotates through the same double-handful of subjects on something like a six week timer. It does get a bit tedious, because there's very little that's actually new to be said, and everyone just rehashes the same tired arguments over and over and over.
"whoever tells you to run the study" is basically whoever approves the grant, so either a business, the government, or a university (indirectly using the governments money). all three are corruptible in their own ways.
businesses certainly have a high incentive to get internal research correct. they don't necessarily have the same incentives when it comes to publishing results or funding external research. see tobacco health research performed/funded by tobacco companies.
in general i trust businesses a bit more than governments, because I find it easier to dissect their motivations, but either can be greatly incentivised to distort scientific findings.
The issue explained in the original article is that Business funds the studies, it turns out they are wrong, and Business still takes care that the wrong results are disseminated.
So I miss how Business being different from University/Government is helpful to even analyze the problem.
Posts like this are often put on hacker news. No one doubts that cherry-picking from hypothesis is real. The same goes for 'spinning' negative results.
However, the solution: "pre-register trials and only do what you say you are going to do" oversimplifies things a lot. Testing and rejecting your hypothesis is a very real part of doing science. But its also a scientists' job to come up with a new hypothesis that explains the data better. I think the real problem here is that writing something up and saying: "our initial hypothesis was wrong, we suggest this and this factor is at play" is not the way science is done currently.
It is not 'oversimplification', but pointing out the traps and pitfalls of empirical validation.
If you gain new hypotheses in the process of validating and falsifying your old ones, you need a second, independent study to validate the new ones. You anyway always run the danger that the result you found is a random artefact of your study participant group. If you validate the new insights with the same group, this risk becomes uncontrollable (e.g., confidence intervals become meaningless in such a setting).
I've been kinda thinking this for more than a decade after working at one of the big pharmas. I witnessed several trials with subpar results that would not go on to be published. I think all studies should undergo a simple national pre-registration and require a summary at the end of each study. One of the things that makes humans special is our ability to store information and pass it to further generations and just throwing away unwanted results is not helping anyone.
I've had an idea about this problem that I'd be happy to hear your thoughts about:
Simply put, a promise for an independant future reproduction study should be part of the published paper.
Once a researcher achieves a publishable result, she looks for a peer-researcher that will commit to perform a pre-determined reproduction study in the near future. This promise is written in the original paper.
This ensures that a negative reproduction would definitely be published. It incentivises the original researcher to not mess too much with the data post-hoc, and to be as helpful as possible to their reproducing peer. The peer gets a citing before writing the paper, and all the help they'd want to get the study done as quickly and easily as possible (q&a, analysis code etc).
Lets look at an example to ferret out some stuff. Assume that the experiment is looking at some disease, like Gastroesophageal reflux disease (GERD) [0]. It's not a glamorous disease, but it's worth looking into. Say you are looking at the way the nervous system interacts with the sphincter to un/control it. Further, you are looking at some specific synapse. Say, also, that you have a mouse model for this as a test bed (incredibly unlikely, btw). You induce GERD in the mice, wait for erosion of the esophagus, sac the mice, and study the synapses, get the results, negative or positive.
How long do you think it'll take a grad student to do this, to get to that point?
1st year is basically wasted, research-wise, as you've got classes and exams. 2nd year is a little better, as you finally understand all the issues with GERD in mice v. humans, the vagal nerves, etc. Still you may be taking classes and you are prepping for your quals. 3rd year is finally when you can get into the nitty-gritty of the experiment. You finally learn how to sac the mice properly, dissect, etc. You fail, a LOT. Lets say, research-wise, you finally have 1 year's worth of 'real' research under your belt.
4th-7th years are ~80% research work, 20% funding search (at ~90hrs/wk of work). The mice cooperate alright, there are breeding issues, random infections in the vivarium, minimal genetic drift, etc. Finally, you can get 'clean' data that other people may actually believe. You've controlled for sex, for food intake, for stomach acidity, for the phase of the moon, for how much coffee is in the room, etc. You've gone half mad getting controls done. You've learned how to dissect the mice carefully, that you can't have coffee for 3 days beforehand to calm your hands down, how to properly positions and craft the micro-pipette tips, how to run all the custom software you've hacked together badly. You've learned a LOT about this tiny portion of a mouse and how to uncover it's secrets. A lot of what you have learned is only applicable to your hands in your lab with your mice.
After, say, 5 years or 'real' research, you find that those neurons that command that particular sphincter of those mice (experimental controls to hell and back) have something to do with GERD. But only to p=0.0482. A positive result, but juuuuust so. You find something to write about and publish. 7 years of your life, and it's just there if you squint at the data a lot. You get out of grad school with a PhD and open a bakery. The research, what you found, is largely forgotten all the same.
Mind you, this is in a stable lab with a grad student with a stable life. No pregnancies, no marriages, no advisor conflict, no sexual harassment, no funding issues, etc.
Now, the parent comment suggests that we should have some other lab come along and replicate the experiment, do the same thing, just to be certain that the 7 years of that grad studen't life were really doing something, not a statistical fluke. How is that going to actually be accomplished?
Say, yeah, you have the funding already set-up via the NIH, fine. Who is going to do that second round of experiments? What grad student is going to get trained up to do someone else's experiments again? How long will it take them to get to that same point, can they even do it the same way? What about their own original research and their career path? Will their advisors be similarly alright with this? Will their life in grad school be just as stable? Who will teach them how to position the electrodes, to dissect the mice, to deal with vivarium issues, to pass their quals?
It's not that the scientists don't want to re-run experiments, it's that doing then is HARD. Technically, yeah, science is not easy. But logistically? Man, even getting one student through grad school is an accomplishment. If you want to re-run each experiment and paper, you somehow have to deal with re-running all the extra j...
This will significantly bias the second study towards getting the same result. Providing help and assistance beyond the paper itself will create experimental controls that are undocumented - assumptions that were shared between researchers but not published in the papers themselves, because humans are bad at that. Further, giving any sort of relationship between the experimenter and the reproducer will taint them - people are friendly and want to see their friends "succeed" - they will taint their own work out of empathy.
Adversarial collaboration has produced some interesting results, and is probably our best bet for settling arguments on topics where results are consistently rejected over methodology. It's done good work on ESP, and shows some promise on priming if anyone will actually sign on.
But that basically requires finding fields with conflicting viewpoints and well-understood methodology spats, which means established debates. This idea would get the same effects - experiment design that's accessible and verifiable - on untested topics, while simultaneously baking replication attempts into initial publication.
The more I think about this, the more impressed I am. It guarantees replications, it guarantees data and methodology availability, and it makes replications a publication-worthy step by making them part of the initial 'success'. It doesn't solve the file drawer or salami slicing problems, but it does huge work to sidestep them by forcing another p<.05 which isn't subject to them. And wildest of all, it might even be acceptable to journals in a way that "publish replications and null results" isn't. Thanks for the most creative approach to the replication crisis I've heard in ages!
64 comments
[ 55.0 ms ] story [ 1886 ms ] threadThe problem starts here. Most researchers would love to show their negative results, they're well aware of the problem. But they need to publish, they need grants, they need money which is outcome independent. They need an alternative reality where negative results and reproducibility studies make money.
As it stands you get money for publishing praise, a lot of industrially sponsored medical research is just "9/10 doctors recommend x" advertising.
We need to instate the rule that only preregistered studies can be published or at least used by the FDA as for decisions.
Right now you can conduct 1000 studies until you find a handful which randomly show the result you want.
There's another core issue which most people miss. In science, you need to publish results AND explain WHY. That last part of WHY is crucial. The amount of work required to prove a negative - or explaining WHY - is very very high and in many cases close to impossible.
Universities want paid grants for money and prestige, so the that's what the researchers go find. I've said this before on here but the solution to this problem is the universities like Harvard and foundations like RWJ which have near infinite money and don't need to operate like this. They need to push forward real research that is reproducible (maybe several times) and shows whatever the data really shows. The researchers who create reproducible studies get bonuses. Again, you get what you optimize for.
I like that idea a lot. And if the study finds something unexpected there should be a thorough explanation why they deviated from the original plan.
That won't help, not by itself. Preregistration helps with "p hacking", the practice of moving the goal posts until some result become significant. A bigger problem remains.
Medicine and Biology accepted the framework of Statistical Hypothesis Inference Testing, where a null hypothesis is rejected at some p-value, usually 0.05. Ignoring many faults of this framework (for example that the alternative hypothesis is not tested at all, that it is a bad caricature of the bad statistics R. A. Fisher introduced, that the numerical outcomes depend on the probability of events that didn't happen, etc.), the logic is that you limit the false positive rate to below the p-value threshold.
Unfortunately, journals consistently reject submission, unless there is a significant p-value somewhere in there. ("Highly significant" is better, even though the term makes no sense.) So if plenty of researchers investigate some random nonsense where the null hypothesis is actually true, 100% of published studies will be spurious results, preregistration or not.
To make progress, this kind of statistics has to go. Journals would have to change their policies, which probably means peer reviewers have to change theirs. I have no idea how to make that happen.
Of course, that's still going to push researchers to change up their techniques for getting false positives. It rewards either covering unexplored domains (so there's no counterexample to your false positive), or exploiting other tricks to manipulate significance in preregistered work.
I don't think existing journals have much hope of improving their practices, honestly. Between their ludicrous financial incentives and ideologues talking "methodological terrorism", that matter seems depressingly settled. But I wonder if there might be hope for creating a counterweight to this?
What happens if Gelman and Khahneman get together to create the Very Prestigious Journal of Replications and the Somewhat Prestigious Journal of Rejected Hypotheses? The first one is neat because it rewards negative results, since they change the state of what's understood - at the very least it might encourage more people to start checking the most influential and most suspicious results. The second thing might be a harder sell, but it could reward comprehensive negative work on key topics (much like Alzheimer's research has heavily consisted of excluding possible pathways). Honestly, "create new prestigious journals from scratch" sounds far easier than "reform existing journals" or "tenure and reward professors for reasons other than publications".
What used to be "prestigious" has come to mean "high impact factor", mostly because funding agencies needed an "objective" way to grant funding, and being run by bureaucrats, they picked impact factor as a measure of scientific success. For a Journal Of Replications to have impact, researchers would have to cite papers about replications. But that's not expected; you cite the original paper, not the one that replicates a result, and you never hear about the one that failed to reproduce a result.
I don't see that approach working, but I'd like to see someone try it.
Yep, this is definitely the biggest weakness for the idea. A journal about replications would probably end up with low impact factor, and wouldn't be able to grab a groundbreaking result to boost its prestige the way some narrow-topic journals have.
My only thought for handling that was alluded to with "Gelman and Kahneman"; maintaining a tolerable reputation and impact factor would probably require leaning on big names and people who are devoted to doing replication work regardless of journal. Gelman, for instance, showed up in PNAS with references when he criticized that godawful "boarding and air rage" study. If we're willing to abuse the process even further, there might be room to publish methodology-of-replication papers in statistical or procedural journals and create further citations that way.
It's not a very good answer, and I don't think it's going to free anyone from "publish or perish". The best I can really hope for is creating a bit of space for talented, skeptical researchers to add replications to their other work without needing to be tenured and entrenched first.
In academia, there are however many tenured professorships with whatever salary, set by largely non-market forces. In Hollywood, there are only so many recognizable stars at a time who can guarantee sales, so their salaries don't really decline no matter how many people vie for their spots. And the same in pro spots, music, politics, Harvard admissions, etc.
And the result is that without adding new jobs or dropping salaries, the people hiring balance the market somehow. Unpaid internships, selling expensive credentials, would-be singers selling hits to existing stars, massive university donations by parents, vicious hazing on football teams, horrifying abuse by casting agents; people who control these 1,000:1 (or higher) seeker-to-slot fields manage to exploit that eagerness to all kinds of horrible ends. [1]
Academia is probably less bad than many of those fields, perhaps because the rewards at the top are less spectacular. But it's not a coincidence that Brian Wansink's big scandal was about pressuring a grad student to find results in null data, or that grad students and postdocs end up working miserable hours to be third author on their own research.
I don't have an answer here, really. But I certainly agree that as long as there are endless ranks of people struggling to make their names, people are going to keep finding ways to get dramatic-looking results, data be damned.
[1] I suspect this stuff really kicks in at several hundred to one or higher. Harvard doesn't reject this percentage, but note that it applies a time-and-money filter before the applications even arrive.
Meaning what?
> I'm imagining something like you have a dataset and you have to upload that dataset to some third party that checks it for it's validity.
The results are what they are. What is 'validity' meant to mean?
> Of course, this is a completely silly idea but I'd love to know if someone has like any tangential related thoughts on this
Quantitative studies are already published with the proper analyses, which are invariably produced 'automatically' using software, not manual methods.
I imagine there might be some value in publishing raw data, though. There may sometimes be questions like privacy, but I don't imagine they'll always be show-stoppers.
> Then you write exactly WHAT you are going to do with the data and then you send the proposed "routines"
this roughly matches up with the idea of "preregistration" of research, i.e. you define and share what your experimental method is going to be before you start looking at the data and performing analysis, to help guard against some unconscious or conscious decisions to adjust the method after you have observed the experimental data.
i've never heard of cos.io before but they're a top hit for me when searching for "preregistration" https://cos.io/prereg/
Andrew Gelman has written quite a lot about related topics in the past (the "replication crisis" - especially in the social sciences, "p hacking", "the garden of forking paths" http://www.stat.columbia.edu/~gelman/research/unpublished/p_... , https://andrewgelman.com/2017/03/09/preregistration-like-ran... )
I quite like how Gelman theoretically frames this in his "forking paths" paper:
It's absurd that reproducing results be any more of a challenge than simply re-running a freely-available program.
Software is unique in that it can be generally be duplicated and executed trivially.
There's no way to make it trivial to reproduce a test on the strength properties of a new ceramic. There is a way to do this for software, and it's rather silly that it isn't standard scientific practice to do so.
I realise I'm taking a strong line here, but I've never seen a good argument against it.
Scientific ‘papers’ are archaic forms of knowledge transfer suited for a time when physical paper was the only way. These days, science would serve us better if we could see everything involved in the process. I don’t want to see only the results, I want to see the whole notebook and all the hurdles along the way. Why can’t we follow the researchers and the accumulation of evidence in real time?
Now, if researchers were encouraged more to describe in detail their process and everything that went right and wrong throughout a study, along with data and algorithms and everything, perhaps as appendices or in supplemental material like blogs or videos etc., and and I find this is what is happening lately, that would be fine, and a nice ideal to strive for.
But realize that scientists are already required to not only perform the study but write about it, and convince every skeptic that they are right, go to conferences and get an article accepted by a journal which can take a year or more. And now add to this that they are required to prepare the data and software for public consumption, make videos and blog posts that describe everything, answer all questions that the public has. Think about all that overhead you are demanding that goes so far above and beyond doing the actual science. It's not small. And they are not paid extra for it, in fact their paycheck is probably half what they could make doing closed science for a for-profit company. Meanwhile their job as an academic is only to explore new ideas and convince their peers of their worth. Why should they go the extra mile, for free, for every member of the public who demands answers and transparency? Sorry, but it's too. much. work.
For people who work in private R&D, like me, we try to keep lab notebooks so that we have records of pretty much everything imagined or tried, warts and all. Sure, it can seem haphazard, unformatted, and not packaged for general consumption. But, it’s meant for collegues anyway, and it fits the purpose.
As for your last paragraph, I totally empathize with your frustrations. But, those seem to be more structural issues with the economics and politics of science and the academies. I certainly would love to see change there, as well. I wish research could be funded in different ways. But, as a consumer of research, I can only really describe my particular use cases.
The introduction section almost always frames the paper with opinions and biases. And, the conclusion section often focuses too heavily on how great the results are (and the author’s prowess) without identifying interesting issues or irregularities encountered in the methodology, data, or outcomes.
I get that publishing is a huge part of a scientist’s career success and for self-promotion, but I see many papers that over emphasize those aspects. Again, I don’t fault them. One can’t easily get funding without a reputation. But, in my idealized (and probably unrealistic) world it would be different.
I do want to stress that I’m not complaining. What I have access to is amazing. But, sometimes I wish I could see it all.
How about writing into a (public) blog, instead of a lab notebook?
I think this idea of let's do every step of science 100% in the open are completely forgetting that science is a social process. Putting things out there has consequences. The onus is on the scientist to verify things before saying them. There is a word for "scientists" who do not. Personally I don't believe that that is something that will change in the next 100 years.
I understand your exhaustion at the idea, truly, but in an era of publicly funded research, the public does have a right to demand transparency for the same through Congress (in America).
That said, a more reasonable level of transparency, post-facto, ought to be sufficient for for most - emails, data, etc. get requested of members of the Congress, for example. Or for a more representative example, take a look at the explanatory efforts of the Federal Reserve and when they go beyond the plain economic research to also provide detailed public transparency.
I don't know about needing to see all the intermediate data, that seems extreme if the methodology is properly described and the raw data is available.
0: https://www.bitss.org/2014/06/13/preregistration-controversy...
1: https://www.apa.org/science/about/psa/2015/08/pre-registrati...
2: https://aspredicted.org/
3: https://osf.io/
4: https://www.psychologicalscience.org/publications/psychologi...
5: https://www.journals.elsevier.com/cortex/news/registered-rep...
This reminds me of an old website, I think it was called Half Baked, where people could (I think anonymously) post just any ridiculous idea for an invention. It was fun to read. Unfortunately I can't find a link.
But man, when I think about it in terms of science and in the more modern context of preprints, it sounds like Flag Planting, Extreme Edition. Even the ML community, who encourage preprint publication more than any other field I know of, have had some pretty heated exchanges about the validity of using that medium for flag planting, and that is when the "flag planting" at least consists of a short paper properly describing an idea, with some rudimentary empirical result and analysis.
So I dunno, it's an intriguing idea, but not without controversy I think.
if you have poor quality equipment and very few trials, the results are going to be all over the place. if you average the whole class's values, you might actually get close.
To free fall one meter on Earth is about .45 seconds.
If you are systematically off and get .35 seconds, you get a gravity of 16m/s^2. If you are systematically off and get .55 seconds, you get a gravity of 6.5m/s^2. It isn't that hard to be systematically off in your button presses by that amount even in ten trials. The noise is huge compared to the signal, and averaging several attempts can only smooth out random noise, not systematic miscalculations of when the ball leaves the table or lands.
I got the second result. I got a bad grade. I learned my lesson. Remarkably every subsequent experiment I ever ran was within ten percent of the real value. My turnaround was truly amazing.
Throw in the issues of funding ( government - political issues, private - corporate issues ) and there is very little incentive for real research. And with the current academic environment at leading institutions like Yale, scientists probably are too afraid to do research honestly on sensitive topics.
Also, isn't this just a rehash of another nytimes article from last year?
https://www.nytimes.com/2017/05/29/upshot/science-needs-a-so...
There are 3 or 4 nytimes articles on the frontpage. At this rate, how long before the entire frontpage is just nytimes? Just redirect hn to nytimes and be done with it?
For Academics- Whoever tells you to run the study.
Which one do you think is more often corrupted for centuries at a time?
If a Business is wrong, they go out of business.
If a University is wrong, they teach it for the next 10 years.
If a Government is wrong, they go forward with the policy until the next regime change.
One of these is different from the rest.
in general i trust businesses a bit more than governments, because I find it easier to dissect their motivations, but either can be greatly incentivised to distort scientific findings.
So I miss how Business being different from University/Government is helpful to even analyze the problem.
However, the solution: "pre-register trials and only do what you say you are going to do" oversimplifies things a lot. Testing and rejecting your hypothesis is a very real part of doing science. But its also a scientists' job to come up with a new hypothesis that explains the data better. I think the real problem here is that writing something up and saying: "our initial hypothesis was wrong, we suggest this and this factor is at play" is not the way science is done currently.
If you gain new hypotheses in the process of validating and falsifying your old ones, you need a second, independent study to validate the new ones. You anyway always run the danger that the result you found is a random artefact of your study participant group. If you validate the new insights with the same group, this risk becomes uncontrollable (e.g., confidence intervals become meaningless in such a setting).
Simply put, a promise for an independant future reproduction study should be part of the published paper.
Once a researcher achieves a publishable result, she looks for a peer-researcher that will commit to perform a pre-determined reproduction study in the near future. This promise is written in the original paper.
This ensures that a negative reproduction would definitely be published. It incentivises the original researcher to not mess too much with the data post-hoc, and to be as helpful as possible to their reproducing peer. The peer gets a citing before writing the paper, and all the help they'd want to get the study done as quickly and easily as possible (q&a, analysis code etc).
How long do you think it'll take a grad student to do this, to get to that point?
1st year is basically wasted, research-wise, as you've got classes and exams. 2nd year is a little better, as you finally understand all the issues with GERD in mice v. humans, the vagal nerves, etc. Still you may be taking classes and you are prepping for your quals. 3rd year is finally when you can get into the nitty-gritty of the experiment. You finally learn how to sac the mice properly, dissect, etc. You fail, a LOT. Lets say, research-wise, you finally have 1 year's worth of 'real' research under your belt.
4th-7th years are ~80% research work, 20% funding search (at ~90hrs/wk of work). The mice cooperate alright, there are breeding issues, random infections in the vivarium, minimal genetic drift, etc. Finally, you can get 'clean' data that other people may actually believe. You've controlled for sex, for food intake, for stomach acidity, for the phase of the moon, for how much coffee is in the room, etc. You've gone half mad getting controls done. You've learned how to dissect the mice carefully, that you can't have coffee for 3 days beforehand to calm your hands down, how to properly positions and craft the micro-pipette tips, how to run all the custom software you've hacked together badly. You've learned a LOT about this tiny portion of a mouse and how to uncover it's secrets. A lot of what you have learned is only applicable to your hands in your lab with your mice.
After, say, 5 years or 'real' research, you find that those neurons that command that particular sphincter of those mice (experimental controls to hell and back) have something to do with GERD. But only to p=0.0482. A positive result, but juuuuust so. You find something to write about and publish. 7 years of your life, and it's just there if you squint at the data a lot. You get out of grad school with a PhD and open a bakery. The research, what you found, is largely forgotten all the same.
Mind you, this is in a stable lab with a grad student with a stable life. No pregnancies, no marriages, no advisor conflict, no sexual harassment, no funding issues, etc.
Now, the parent comment suggests that we should have some other lab come along and replicate the experiment, do the same thing, just to be certain that the 7 years of that grad studen't life were really doing something, not a statistical fluke. How is that going to actually be accomplished?
Say, yeah, you have the funding already set-up via the NIH, fine. Who is going to do that second round of experiments? What grad student is going to get trained up to do someone else's experiments again? How long will it take them to get to that same point, can they even do it the same way? What about their own original research and their career path? Will their advisors be similarly alright with this? Will their life in grad school be just as stable? Who will teach them how to position the electrodes, to dissect the mice, to deal with vivarium issues, to pass their quals?
It's not that the scientists don't want to re-run experiments, it's that doing then is HARD. Technically, yeah, science is not easy. But logistically? Man, even getting one student through grad school is an accomplishment. If you want to re-run each experiment and paper, you somehow have to deal with re-running all the extra j...
Adversarial collaboration has produced some interesting results, and is probably our best bet for settling arguments on topics where results are consistently rejected over methodology. It's done good work on ESP, and shows some promise on priming if anyone will actually sign on.
But that basically requires finding fields with conflicting viewpoints and well-understood methodology spats, which means established debates. This idea would get the same effects - experiment design that's accessible and verifiable - on untested topics, while simultaneously baking replication attempts into initial publication.
The more I think about this, the more impressed I am. It guarantees replications, it guarantees data and methodology availability, and it makes replications a publication-worthy step by making them part of the initial 'success'. It doesn't solve the file drawer or salami slicing problems, but it does huge work to sidestep them by forcing another p<.05 which isn't subject to them. And wildest of all, it might even be acceptable to journals in a way that "publish replications and null results" isn't. Thanks for the most creative approach to the replication crisis I've heard in ages!