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Reproducibility Crisis Timeline: Milestones in Tackling Research Reliability

Cartoon about science not being self-correcting


It’s not a new story, although “the reproducibility crisis” may seem to be. For life sciences, I think it started in the late 1950s. Large-scale problems in clinical research burst into the open in a very public way then.

But before we get to that, what is “research reproducibility”? It’s a euphemism for unreliable research or research reporting. Steve Goodman and colleagues (2016) say 3 dimensions of science that affect reliability are at play:

  • Methods reproducibility – enough detail available to enable a study to be repeated;
  • Results reproducibility – the findings are replicated by others;
  • Inferential reproducibility – similar conclusions are drawn about results, which brings statistics and interpretation squarely into the mix.

That doesn’t cover everything, for example, the reproducibility of the materials used in laboratory research.

There is a lot of history behind each of those. Here are some of the milestones in awareness and proposed solutions that stick out for me.




Estes Kefauver was a U.S. Senator and Adlai Stevenson’s presidential running mate. He had become famous at the start of the decade with hearings into organized crime. More than 30 million people watched some of those hearings, on television or free in movie theaters.

He turned his attention to the pharmaceutical industry at the end of the decade, holding hearings into drug prices in 1958 and 1959. One of the issues that emerged was the “sorry state of science supporting drug effectiveness”. This outcry about research reproducibility led to a major change in research requirements for FDA approval in 1962.

Part of the problem’s solution had a major milestone in 1959, too. Austin Bradford Hill led a meeting in Vienna that codified the methodology for controlled clinical trials.

Earlier in the 1950s, though, there was a development that stands as a milestone in fueling science’s reproducibility crisis by inadvertently introducing a perverse incentive: Eugene Garfield proposed the journal impact factor in 1955.




In 1962, the Kefauver-Harris amendments required “adequate and well-controlled clinical investigations” for FDA approval: adequate was at least 2 studies – a major step in expecting replication of results.

A new problem in biological research was revealed in 1966 at a conference in Bethesda. Stanley Gartler was the first to report contamination in cell lines in cancer research (reported in Nature1968). Still not adequately dealt with, that’s grown into a juggernaut of un-reproducibility, making thousands of studies unreliable.

That year also saw what may be the first example of the science of systematically studying science’s methods – what John Ioannidis and colleagues have dubbed meta-research. It was a study of statistics and methods of evaluation in medical journal publications (discussed here).




The 70s brought us 2 key methods: systematically reviewing evidence (1971) and meta-analysis: a way to analyze the results of several studies at once (1976) (explainer here). Those methods didn’t just help make sense of bodies of evidence. They also propelled meta-research.


Cartoon meta-analysis


And 1977 surfaced a problem in scientists’ behavior that allows unreliable scientific findings to take root and thrive. Michael Mahoney showed confirmation bias thrived in peer review:

Confirmatory bias is the tendency to emphasize and believe experiences which support one’s views and to ignore or discredit those which do not…[R]eviewers were strongly biased against manuscripts which reported results contrary to their theoretical perspective.




Analyzing the reliability of studies took a formal step forward in 1981, with the publication of a method for assessing the quality of clinical trials.

Doug Altman and colleagues took on the issue of problems with the use and interpretation of statistics, with 1983 statistical guidelines for medical journals.

And a way forward was proposed for the problem of unpublished research results. The unpublished research results are often the disappointing ones. That leaves us with a deceptive public record of science.

John Simes called for an international registry of clinical trials in 1986. Registering the details of all research before it is actually done would mean we could at least identify gaps in the published research record down the line.




According to Goodman & co (2016), the term “reproducible research” was coined in 1992. Computer scientist Jon Claerbout used it in the sense of methods reproducibility – enough published details for someone else to be able to reproduce the steps of a study.

Formal standardized guidelines for reporting research – one of the key strategies for trying to improve research reproducibility – arrived in clinical research in the 1990s. The CONSORT statement for clinical trials in 1996 is the milestone here.




The registration of clinical trials at inception took a giant leap forward in 2004 when the International Committee of Medical Journal Editors (ICMJE) announced they would not publish a trial that had not been registered.

“Why most research findings are false” landed like a bomb on science’s landscape in 2005. John Ioannidis’ paper has now been viewed more than 1.8 million times, and definitely counts as a milestone in awareness of science’s reproducibility problems. (I wrote about the article and controversies around it here.)

In 2007, FDAA, the FDA amendments act, added public results reporting to an earlier requirement that drug clinical trials be registered at inception. Final Rules and NIH policies that give those requirements teeth go into effect in January 2017.




Pre-clinical research got a major jolt in 2012, when Begley and Ellis at the biotech company Amgen set out to confirm cancer research findings:

Fifty-three papers were deemed ‘landmark’ studies…[S]cientific findings were confirmed in only 6 (11%) cases. Even knowing the limitations of preclinical research, this was a shocking result.

In 2013, registering studies at inception took a leap at the journal Cortex with registered reports. Registered reports are peer reviewed detailed protocols, with the journal’s commitment to publishing the results after the study is completed. (A tally of journals following suit is kept here.)

In 2014, the NIH began reporting on its strategies for addressing reproducibility, including reporting guidelines for preclinical research, and PubMed Commons, which had arrived in 2013. That’s the commenting system in PubMed, the largest biomedical literature database.

Psychology’s big jolt came in 2015, when the Open Science Collaboration reported that they replicated between a third and a half of 100 experiments and correlation studies.

And in 2016, the American Statistical Association (ASA) issued its first-ever guidance, trying to stem the tide of misuse and misinterpretation of p values. (Explainer here.)

2016 is ending, though, with a potential roll-back in the clinical research rigor and transparency required for FDA approval. Lesser levels of evidence than adequately controlled clinical trials might be back, and full raw data might not be necessary, either.

We have a “reproducibility crisis” because we need to do more to try to prevent bias in research design, conduct, interpretation, and reporting. And after that we need others to interrogate what’s found and replicate it in different contexts. As Christie Aschwanden points out, that’s just plain hard to do. But “science” isn’t really scientific without all of that, is it?



Disclosure: PubMed Commons is part of my day job.

If you’re interested in the history of improving the reliability of clinical research, the James Lind Library is a goldmine. I drew on it heavily to develop this post.

Updates on 6 December 2016: Added materials reproducibility – thanks to Joanne Kamens for pointing out this gap in the definition I used on Twitter.

Andrew Gelman has a reproducibility timeline for psychology (and it has very little overlap with mine).


The cartoons and illustrations are my own (CC-NC-ND-SA license). (More cartoons at Statistically Funny and on Tumblr.) 


* The thoughts Hilda Bastian expresses here at Absolutely Maybe are personal, and do not necessarily reflect the views of the National Institutes of Health or the U.S. Department of Health and Human Services.



  1. Thanks for a fascinating, if brief, survey of the history.

    I’d put the recognition of the need for reproducibility much earlier. It was explicit in Fisher’s 1926 statement that

    “Personally, the writer prefers to set a low standard of significance at the 5 percent point. . . . A scientific fact should be regarded as experimentally established only if a properly designed experiment rarely fails to give this level of significance”

    The bit about “rarely fails” was quickly forgotten, and that is surely part of the problem. I doubt that this is the first statement about the need for replication.

    Another problem has been the near-total failure of statisticians to agree about the principles of inference. In 1971 I said “It is difficult to give a consensus of informed opinion because, although there is much informed opinion, there is rather little consensus”. That’s almost as true now as it was then.

  2. Thanks, David. Yes, I agree there would be lots of statements about the need for replication and so on. But I haven’t yet seen anything else earlier that’s a public criticism of unreliable criticism outside the profession, which is why I picked the Kefauver hearings as the start.

    I hadn’t read the part of Andrew Gelman’s post that was a reproducibility timeline before I wrote this. He picked completely different things – more granular, and neuroscience/psychology-focused. One of his, raising the papers dubbing “researcher degrees of freedom” and “p-hacking” had a wide impact, I agree. And your paper certainly fits in that mould too – but I just stuck with the ASA statement to stand for that set of concerns. Yes, it’s the problem of brevity – but I think brevity has strengths too.

  3. As we focus on issues with statistics in psychology, I suspect that another crisis is already in the making. Machine learning is having a huge impact on neuroscience, with countless papers that use a variety of pattern classifiers in large EEG, MEG, and fMRI data sets. Unfortunately the enthusiasm for these approaches is often not accompanied by appropriate caution, since there is a misplaced faith in their statistical rigor.

    As the computer science and physics disciplines can teach us, big data sets are extremely dangerous to make inferences from because of the dangers of overfitting when designing an analysis. Many people think that cross-validation is sufficient protection but it really isn’t. If you’d like to learn more about this, we’ve got a preprint on biorxiv that illustrates this issue by showing how easy it is to train a classifier to detects patterns that aren’t there, even with the use of cross validation.

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