Category Archives: Biostatistics

A branch of statistics with a focus on biological systems — in my case almost always human health.

Campbell and Stanley explained replication rates in 1963

Over 60 years ago, Donald Campbell and Julian Stanley published their classic, slim volume Experimental and Quasi-Experimental Designs for Research. One of their earliest observations concerns the trade-off between internal and external validity. Specifically, the more precisely one can establish a causal relationship, the less one can say about its generality. In recent work, I show that simultaneously maximising internal and external validity is not merely a practical limitation to be mitigated, but a structural impossibility. The relationship is analogous to the Heisenberg uncertainty principle that shows one cannot simultaneously know both the position and momentum of a particle with arbitrary precision. In the context of the social and behavioural sciences, the more precisely one identifies a cause, the narrower the domain to which that knowledge applies.

I reviewed this problem in terms of the so-called “replication crisis”, the difficulty researchers have encountered in replicating published causal findings. Shortly after posting that paper, Nature published a series of articles on research credibility, including a large-scale investigation of replicability in the social and behavioural sciences. The empirical effort is extraordinary, involving hundreds of researchers and a substantial coordination infrastructure. The methods, results, and theoretical framing are all of considerable interest. However, the study has also generated headline figures that are readily misinterpreted—an outcome encouraged both by editorial framing and by the structure of the paper itself.

The central difficulty lies in two under-specified concepts that drive the research. The replication is of the “same question” and the “claim”. Whether a replication tests the “same question” is treated as a local, theory-laden judgement made by individual teams. Sameness is treated as constant at two levels simultaneously. First the multiple replications of a single study should be replicating the same thing, as if each attempt stood in an identical relationship to the original. And across all the original studies, the idea of sameness should stand in an identical relationship between a replication and its target regardless of which study is being replicated. If “same” does not mean the equivalent thing within and between replications, the target drifts meaninglessly

At the same time, replications are of “claims” which are scientific claims reduced to directional empirical statements, detached from the estimands, models, and analytic pipelines. That is, the claim is detached from the scientific meaning that gave it purchase in the original study. The same problem with “claims” arose in the team’s Nature paper on analytic robusteness. Abstracting scientific claims into more generic “claims” produces a mismatch between design and inference. Heterogeneous interpretations of what is actually being tested are collapsed into standardised statistical comparisons. Apparent agreement or disagreement may therefore reflect shifts in underlying targets rather than genuine replication or failure.

A related issue is that the study attempts to straddle internal and external validity without resolving their tension. It presents itself as assessing whether findings replicate, but in practice examines how results behave under modest variation in context, measurement, and implementation—something closer to robustness or transportability than strict replication. The use of multiple, non-equivalent metrics of “success” in the Nature article reinforces this ambiguity. Replication rates vary substantially depending on the criterion, yet a single headline figure is foregrounded: “Half of social-science studies fail replication test in years-long project“. The result is a study that is informative about the behaviour of findings (and researchers) under perturbation, but is easily—and predictably—read as making stronger claims about the reliability or truth of scientific results than its design can support.

Underlying both issues is a deeper disagreement about what replication is for. The paper’s opening paragraph explicitly reflects this tension. One reference is the National Academies of Sciences (NAS) report, which defines replication in procedural and statistical terms. Collect new data using similar methods and assess whether results are consistent, typically via effect sizes and uncertainty intervals. The other reference is a 2020 PLoS Biology article by Nosek and Errington (the two senior authors of this Nature paper), who argue that the NAS definition is not merely imprecise but conceptually mistaken. On the Nosek-Errington account, determining that a study is a replication is a theoretical commitment. Both confirming and disconfirming outcomes must be treated in advance as diagnostic of the original claim. The Nature paper adopts this language—replication teams were instructed to produce “good faith tests” of claims—but the article reports results entirely using metrics derived from the procedural-statistical tradition of NAS. This is not a superficial inconsistency. The two frameworks imply different standards of success, different interpretations of failure, and different meanings for any aggregated replication rate. The headline figures that have circulated are products of the latter framework; whether they would survive translation into the former is not addressed.

It is here that Campbell and Stanley’s observation, and its formalisation, becomes decisive. The procedural-statistical approach implicitly treats internal validity as primary and assumes that external validity can be inferred from it. That is, if results are consistent, the finding travels. The structural trade-off shows that this assumption cannot hold. The very steps taken to secure internal validity constrain the scope of generalisation. A high replication rate under this framework may therefore be simultaneously informative and misleading. It indicates that a result can be reproduced under sufficiently similar conditions, while obscuring how narrow those conditions may be. The Nosek-Errington framework recognises the need for theoretical commitment, but without a principled account of causal structure it cannot resolve the tension either. What the Nature paper ultimately demonstrates—perhaps inadvertently—is that replicability is not a property of findings alone. It is a property of the relationship between a finding and the conditions under which it is tested. This underscores a Cartwrightian notion of relationships tied to particular material configurations–nomological machines. Until that relationship is made explicit, headline replication rates will continue to invite overconfident conclusions in both directions and admonitions for better methods.

I did not have access to the published article which is behind the Springer-Nature paywall. Instead I relied on the publicly available preprint.

Analytic robustness could be a real problem

A recent article in Nature on the robustness of research findings in the social and behavioural sciences found that only 34% of re-analyses of the data yielded the same result as the original report. This sounds horrible. It sounds like two-thirds of the research that social and behavioural scientists are doing is low quality work, and certainly does not deserve to be published. One might reasonably ask if “confabulist” rather than “scientist” might not be a better job title.

Unfortunately, the edifice of “robust research” has been built on foundations of sand. The research shares many of the weaknesses of another article recently published in Science Advances, which I discuss here. There is little that can be concluded from the research that could actually inform scientific practice nor permit any observation about the quality or robustness of the original articles. It does, however, say something of interest for sociologists of science about the diversity of views that researchers have about how to re-analyse data to address conceptual claims.

The procedure followed in the Nature article was described thus.

To explore the robustness of published claims, we selected a key claim from each of our 100 studies, in which the authors provided evidence for a (directional) effect. We presented each empirical claim to at least five analysts along with the original data and asked them to analyse the data to examine the claim, following their best judgement and report only their main result. The analysts were encouraged to analyse those studies where they saw the greatest relevance of their expertise.

The word “claim” here does a lot of work. One might reasonably argue that a scientific claim in a published article is a statement of finding in the context of the hypothesis, the model, the analytic process, and the results. But this is not what is meant here. That full scientific sense of a claim is closer to what the Centre for Open Science team use as a starting point for a separate article on “reproducible” research. In the context of this article a “claim” is some vaguer statement of finding. It is an isolated single claim, has a direction of effect, and critically, is “phrased on a conceptual and not statistical level”.

The conceptual claim is closer to a vernacular claim. It is closer to the kind of thing you might say at a dinner party or read in the popular science section of a magazine. Something like, “did you hear that single female students report lower desired salaries when they think their classmates can see their preferences?” (Claim 025).

Under this framework, one should be able to abstract a full scientific claim into a conceptual claim, and if the conceptual claim is robust, independent scientists analysing the same data, making equally sensible choices about the analysis of the data, will converge on the conceptual claim. The challenge is that your pool of independent and equally sensible scientists need to agree with each other (without consultation) how that conceptual claim is to be translated into a scientific claim. A part of the science is deciding on the estimand for testing the claim, but the estimand is fixed by the analytic choice not by the conceptual claim. If two scientist analyse the same dataset but target different estimands through their analytic choices, they are not converging on the same conceptual claim. Against all logic, an analytic schema targeting a different estimand that nonetheless produces an estimate close to the estimate of the original paper, supports the robustness of the paper.

The framework, therefore, has a double incoherence. First, divergence of estimates (between the original analysis and re-analysis) is misread as fragility when it may simply reflect different estimands—different scientists sensibly translating the conceptual claim into different scientific claims. Second, and more damaging, convergence is misread as robustness when it may be entirely spurious—two analysts targeting different estimands who happen to produce similar point estimates are not confirming each other. They’re producing agreement by accident, across questions that aren’t the same question.

So the framework is wrong in both directions simultaneously. It penalises legitimate scientific pluralism and rewards numerical coincidence. A study could score as highly robust because several analysts happened to get similar numbers while asking entirely different questions. A study could score as fragile because several analysts made defensible but divergent estimand-constituting choices that led to genuinely different answers to genuinely different questions.

There is another an far more interesting reading of this paper, which has neither a click-bait quality nor the opportunity to remonstrate. Where the authors have identified fragility (or a lack of robustness), another could legitimately and positively see vitality and methodological pluralism. The social and behavioural sciences work in the messy space of self-referential agents actively interacting with and changing the environments in which they live and do science. It is hardly surprising that epistemic pluralism is a consequence of this. The 34% figure is not a scandal. It is valuable (under appreciated) data about the nature of social reality.

I did not have access to the published article which is behind the Springer-Nature paywall. Instead I relied on the publicly available preprint.

Parsing the NIH Reform Debate

I was recently alerted to Martin Kulldorff’s Blueprint for NIH Reform — a document that’s stirred some intense reactions among my colleagues. A few view it as a needed critique of systemic inefficiencies. Most regard it as an ideological Trojan horse—an attack on science dressed as reform. So where does the truth lie?

The short answer is: it’s complicated—and the messenger matters.

Kulldorff, once a Harvard professor and biostatistician, became a polarising figure during the COVID-19 pandemic for promoting ideas widely dismissed by the mainstream scientific community, including opposition to lockdowns, masking, and even some aspects of vaccination policy. He was also a co-author of the controversial Great Barrington Declaration, which called for herd immunity through natural infection — a strategy many experts considered unscientific and dangerous at the time.

This background understandably colors how his recent proposals are received.

But here’s the nuance: the Blueprint itself raises a number of ideas that aren’t inherently fringe. Calls for reforming NIH grant structures, enhancing academic freedom, incentivising open science, and streamlining peer review are echoed by many researchers across disciplines — including those with no ties to politicised public health debates. Frustrations with bureaucratic inefficiencies and perverse incentives in scientific funding are real and shared.

Where it becomes tricky is in the framing. Kulldorff doesn’t just argue for reform — he implies that current structures are suppressing truth, and that controversial views (like his own during the pandemic) have been silenced not because they lack merit, but because of groupthink or institutional bias. That framing, for many, crosses the line from constructive critique into undermining the scientific process itself.

There’s also a risk that pushing for more “openness” in what research gets funded — while laudable in theory — could result in resources being diverted to low-evidence, high-noise pursuits. Or, as one colleague aptly put it, “sending the ferret down an empty warren.” Science thrives on curiosity, but it also requires discipline and evidence-based filters.

Venue choice also matters. If this proposal were intended as a serious intervention into science policy, it might have been published in a mainstream medical or policy journal where it could be openly debated across the full spectrum of scientific opinion. Instead, it was published in the Journal of the Academy of Public Health — a platform co-founded and edited by Kulldorff himself, with close ties to politically conservative and contrarian public health figures. That choice raises questions about whether the article is seeking reform through consensus, or carving out space for alternative narratives that have struggled to find support in mainstream science.

So how should we engage with this?

Acknowledge the valid points: There is room — and need — for reform in how science is funded, reviewed, and communicated.
Be vigilant about context: Not all calls for reform are neutral. Motivations and affiliations matter, especially when public trust is on the line.
Defend the integrity of science: We can advocate for better systems without abandoning the core principles of evidence, rigor, and accountability — including fair peer review and a balance of risk and reward.

In the end, this is not a binary question of “pro-science” vs “anti-science.” It’s about how science evolves, who gets to shape that evolution, and what values we prioritise along the way — openness, yes, but always in service of evidence and public good.

This is an independent submission, edited by D.D. Reidpath.

What is the optimal number of broken jaws?

I was chatting with a friend recently about the COVID-19 response in different countries. Reflecting on her own country, she said, “It is so hard to know what is right!”; that is, it is so hard to know what the right response to COVID-19 should be.

The variation, for instance, in countries’ lockdown responses is substantial, but which country is doing the right thing? In some countries, there has been no lockdown. The government asked the people to be sensible. In other countries, the government legally confined people to their homes — only one person was allowed out at very specific (restricted) times to buy essentials. Given these two policy extremes (be sensible and house arrest), which one is the right one, and how do you know?

An economist, I have forgotten who once asked tongue-in-cheek, what is the optimal number of dead babies? The very purpose of such a crass question is to make you stop and think. What tradeoffs are you prepared to make to save the lives of babies? Sure, you could be lazy, condemn the questioner as immoral (for even asking you to think), and declare zero dead babies to be the right number. As a simple policy proposition, if zero dead babies is the right number, then all the resources of society should be aimed at preventing neonatal deaths. ALL RESOURCES! Until the policy goal has been achieved, there is more work to be done to reduce the number. One dead baby is too many!!! Farmers may farm, but only to produce the food that supports the workforce that is striving to reduce baby deaths to zero. Teachers may teach, but only to educate the people to fill the jobs to support the policy goal to reduce baby deaths to zero. There is very limited use for art, music, cinema, sport, fashion, restaurants, etc. They will all have to go! If five-year-old deaths increase, that is something to live with, just as long as we can save another baby.

At this point, you’re probably thinking, well that’s stupid. That’s not what I meant when I said the optimal number of dead babies is zero. What I meant was something more along the lines of, “In an ideal world there would be zero dead babies”. Equally, if you were asked about poverty or crime, or amazing works of art, you presumably would have stated the ideals in terms of zero poverty, zero crime, and lots more wonderful art. And this is quite a different proposition. An ideal world is not ideal in virtue of its achievement of a single goal. It is ideal in having achieved all sorts of different outcomes. And that is why the real and the ideal do not intersect. In the real world, we do not achieve the ideal anything. We seek to achieve many ideals, and realistically, we hope to make progress against them, knowing that there is always more to be done. In striving to improve the societal position against a basket of goals, we allocate limited resources and make trade-offs.

This is one part of the COVID-19 problem, and, as my friend observed, why it is so hard to know what is right. What is the right number of COVID-19 deaths? There are lots of important, rational debates to be had around this topic because it is about the tradeoffs we are prepared to make against a basket of societal goals against the myopic achievement of one. Muscular public health responses — effective house arrest — are very good at reducing the number of new COVID-19 cases. They are also very effective at increasing domestic violence, increasing depression, lowering child immunisation rates, degrading child education, increasing poverty and increasing unemployment. If the societal goal should be zero COVID-19 deaths, what is the optimal number of broken jaws, suicide attempts, measles encephalitis cases, illiterate and enumerate children, beggars, and soup kitchens?

All these issues, under normal circumstances, are things of concern to Public Health and maybe, one day, they will be again.

Another part of the COVID-19 problem is that, whether a government “did the right thing” will be determined in hindsight, and by making (inadequate) historical comparisons between the outcomes across countries’. In democracies, at least in the short-term, “did the government do the right thing?” will often be decided at the ballot box. This will surely get the answer wrong. In less-than-democracies, astute rulers will write the history books themselves ensuring that, without regard to the outcome, the government did the right thing.

One of the main reasons that “it is so hard to know what is right!” is that we rarely have a societal view about the long term goals we wish to achieve and the tradeoffs we are prepared to make. Furthermore, we are reluctant to accept the fact that one can do the right thing and still fail. We assume that the right course of action will, by definition, result in success. We are prospective Kantians and retrospective Utilitarians.