Category Archives: Research

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.

Ideology and the Illusion of Disagreement in Empirical Research

There is deep scepticism about the honesty of researchers and their capacity to say things that are true about the world. If one could demonstrate that their interpretation of data was motivated by their ideology, that would be powerful evidence for the distrust. A recent paper in Science Advances ostensibly showed just that. The authors, Borjas and Breznau (B&B), re-analysed data from a large experiment designed to study researchers. The researcher-participants were each given the same dataset and asked to analyse it to answer the same question: “Does immigration affect public support for social welfare programs?” Before conducting any analysis of the data, participant-researchers also reported their own views on immigration policy, ranging from very anti- to very pro-immigration. B&B reasoned that, if everyone was answering the same question, they would be able to infer something about the impact of prior ideological commitments on the interpretation of the data.

Each team independently chose how to operationalise variables, select sub-samples from the data, and specify statistical models to answer the question, which resulted in over a thousand distinct regression estimates. B&B use the observed diversity of modelling choices as data, and examined how the research process unfolded, as well as the relationship of the answers to the question and researcher-participants’ prior views on immigration.

B&B suggested that participant-researchers with moderate prior views on immigration find the truth–although they never actually say it that cleanly. Indeed, in the Methods and Results they demonstrate appropriate caution about making causal claims. However, from the Title through to the Discussion, the narrative framing is that immoderate ideology distorts interpretation—and this is exactly the question their research does not and cannot answer—by design.

Readers of the paper did not miss the narrative spin in which B&B shrouded their more cautious science. Within a few days of publication, the paper had collected hundreds of posts and it was picked up in international news feeds and blogs. Commentaries tended to frame pro-immigration positions as more ideologically suspect.

There are significant problems with the B&B study, however, which are missed or not afforded sufficient salience. To understand the problems more clearly, it helps to step away from immigration altogether and consider a simpler case. Suppose researchers are given the same dataset and asked to answer the question: “Do smaller class sizes improve student outcomes?” The data they are given includes class size, test scores, and graduation rates (a proxy for student outcomes). On the surface, this looks like a single empirical question posed to multiple researchers using the same data.

Now introduce a variable that is both substantively central and methodologically ambiguous, a measure of the students’ socio-economic disadvantage. Some researchers treat socio-economic disadvantage as a covariate, adjusting for baseline differences to estimate an average effect of class size across all students. Others restrict the sample to disadvantaged pupils, on the grounds that education policy is primarily about remediation or equity. Still others model heterogeneity explicitly, asking whether smaller classes matter more for some students than for others. Each of these choices is orthodox. None involves questionable practice, and all of them are “answering” the same surface question. But each corresponds to a different definition of the effect being studied and, most precisely, to a different question being answered. By definition, different models answer different questions.

In this setting, differences between researchers analyses would not normally be described as researchers answering the same question differently. Nor would we infer that analysts who focus on disadvantaged students are “biased” toward finding larger effects, or that those estimating population averages are distorting inference. We would recognise instead that the original prompt was under-specified, and that researchers made reasonable—if normatively loaded—decisions about which policy effect should be evaluated. B&B explicitly acknowledge this problem in their own work, writing: “[a]lthough it would be of interest to conduct a study of exactly how researchers end up using a specific ‘preferred’ specification, the experimental data do not allow examination of this crucial question” (p. 5). Even with this insight, however, they persist with the fiction that the researchers were indeed answering the same question, treating two different “preferred specifications” as if they answer the same question. It would be like our educationalists treating an analysis of outcomes for children from socio-economically deprived families as if answered the same question as an analysis that included all family types.

B&B’s immigration experiment goes a step further, and in doing so introduces an additional complication. Participant-researchers’ prior policy positions on immigration are elicited in advance of their data analysis, and then B&B used that as an organising variable in their analysis of participant-researchers.

Imagine a parallel design in the education case. Before analysing the data, researchers are asked whether they believe differences in educational outcome are primarily driven by school resources or by family deprivation. Their subsequent modelling choices—whether to focus on disadvantaged pupils, whether to emphasise average effects, whether to model strong heterogeneity—are then correlated with these priors. Such correlations would be unsurprising. If you think disadvantage is more important than school resources to student outcomes, you may well focus your analysis on students from deprived backgrounds. It would be a mistake, however, to conclude that researchers with strong views are biasing results, rather than pursuing different, defensible conceptions of the policy problem.

Once prior beliefs are foregrounded in this way, a basic ambiguity arises. Are we observing ideologically distorted inferences over the same shared question, or systematic differences in the questions being addressed given an under-specified prompt? Without agreement on what effect the analysis is meant to capture, those two interpretations cannot be disentangled. Conditioning on ideology (as B&B did) therefore risks converting a problem of an under-specified prompt into a story about ideologically biased reasoning. This critique does not deny that motivated reasoning exists, or that B&B’s research-participants were engaged in it. They simply do not show it, and the alternative explanation is more parsimonious.

The problems with the B&B paper are compounded when they attempt to measure “research quality” through peer evaluations. Researcher-participants in the experiment are asked to assess the quality of one another’s modelling strategies, introducing a second and distinct issue. The evaluation process is confounded by the distribution of views within the researcher-participant pool.

To see this, return again to the education example. Suppose researchers’ views about the importance of family deprivation for educational outcomes are normally distributed, with most clustered around a moderate position and fewer at the extremes. A randomly selected researcher asked to evaluate another randomly selected researcher will, with high probability, be paired with someone holding broadly similar views (around the middle of the distribution). In such cases, the modelling choices are likely to appear reasonable and well motivated, and to receive high quality scores. The evaluation implicitly invites the following reasoning: “your doing something similar to what I was doing, and I was doing high quality research, therefore you must be doing high quality research as well”.

By contrast, models produced by researchers in the tails of the distribution will more often be evaluated by researchers further away from their ideological view. Those models may be judged as poorly framed or unbalanced—not because they violate statistical standards, but because they depart from the modal conception of what the broadly framed question is about. Under these conditions, lower average quality scores for researchers with more extreme priors may reflect distance from the dominant framing, not inferior analytical practice. B&B, however, argued the results show that being ideologically in the middle produced higher quality research.

The issue here is not bias but design. When both peer reviewers and reviewees are drawn from the same population, and when quality is assessed without a fixed external benchmark for what counts as a good answer to the question, peer scores inevitably track conformity to the field’s modal worldview. Interpreting these scores as evidence that ideology degrades research quality is wrong.

B&B’s paper is useful. It shows that ideological commitments are associated with the questions that researchers answer. Cleanly, that is as far as it goes. Researchers answer the questions they think are important. The small, accurate interpretation is not as impressive a finding as “ideology drives interpretation”, but B&B’s research is most valuable where it is most restrained. The further it moves from firm ground describing correlations in researchers’ modelling choices towards the quick-sand of diagnosing ideological distortion of inference, the worse it gets. What they present as evidence of bias is more reasonably understood as evidence that their framing question itself was never well defined. Through its narrative style, and not withstanding quiet abjurations against causal inference, the paper invites the conclusion that researchers working on a divisive, politically salient topics simply find what their ideologies lead them to find. And taken at face-value, it licenses the distrust of empirical research on contested policy questions.

On becoming a decolonial scholar

I have observed some early, tentative steps of young academics to become world-class decolonial scholars in global health. This is a rich and rewarding area of endeavour that has real potential to launch a career without the baggage of narrow disciplinary boundaries, rigid methodological commitments, or premature demands for epistemic closure. When approached carefully, decolonial scholarship allows emerging researchers to engage critically with power, history, and knowledge while retaining considerable flexibility in analytic approach. What follows is offered as practical guidance for those who wish to navigate this space with confidence and coherence.

Decolonising global health has become a central ethical orientation for contemporary scholarship in the field. For early-career researchers, the challenge is not whether to adopt a decolonial stance, but how to do so convincingly within existing academic norms. You do not want a piece buried in the Malawi Medical Journal when global recognition can be found in The Lancet, PLOS, or BMJ. This brief guide offers practical advice on positioning oneself as a decolonising scholar, drawing on common techniques that are widely recognised as markers of both epistemic and moral alignment.

A successful decolonial paper begins with the scholar rather than the question. Reflexive positioning statements have become an essential opening move, allowing authors to locate themselves within global hierarchies of power, privilege, and complicity. Personal proximity to marginalisation is an asset. These declarations are most effective when they are candid yet indeterminate, signalling awareness without constraining interpretation. Once positionality has been established, subsequent analytic choices are more readily received as ethically grounded rather than methodologically contingent.

Research problems should then be framed in historical or structural terms rather than as empirical hypotheses. Questions that invite falsification risk reintroducing evaluative standards associated with dominant epistemic traditions linked to globalised practice. By contrast, concepts such as colonial residue, epistemic silencing, or inherited injustice resist closure and encourage moral elaboration. Where findings introduce ambiguity or contradiction, this can be interpreted not as analytic weakness but as evidence of the complexity produced by colonial histories themselves.

Within this framing, epistemic injustice can be treated as an outcome rather than a proposition requiring demonstration. The presence of asymmetry—between disciplines, regions, or forms of expertise—may be taken as sufficient indication of harm. Distinguishing between the unjust exclusion of valid insight and the justified rejection of erroneous claims is rarely necessary and may inadvertently reinscribe colonial distinctions between knowledge and belief. Moral recognition, once granted, does much of the epistemic work.

Lived experience occupies a privileged place in this literature and should be elevated accordingly. Personal and communal narratives can be used generously as data, though care should be taken to avoid subjecting them to processes such as validation, triangulation, or comparative assessment. Such techniques imply the possibility of error, which sits uneasily with commitments to epistemic plurality. Where accounts conflict, the tension may be presented as evidence of multiple ways of knowing rather than as a problem requiring resolution.

Ontological language offers particular flexibility. Early declaration of commitment to multiple ontologies allows scholars to accommodate divergent claims without adjudication. Later, when universal commitments are invoked—such as equity, justice, or health for all—these can be treated as ethical aspirations rather than propositions dependent on a shared reality. The absence of an explicit bridge between ontological plurality and universal goals rarely attracts critical scrutiny.

Power should be rendered visible throughout the paper, though preferably without becoming too specific. Abstractions such as “Western science”, “biomedicine”, or “the Global North” serve as effective explanatory devices while minimising the risk of implicating proximate institutions, funding structures, or professional incentives. Authorship practices, by contrast, provide a concrete and manageable site for decolonial intervention, often with greater symbolic return than methodological reform.

Papers should conclude with a call for transformation that exceeds immediate implementation. Appeals to reimagining, unsettling, or dismantling signal seriousness of intent, while the absence of operational detail preserves the moral horizon of the work. Evaluation frameworks, metrics, and timelines may be deferred as future tasks, once the appropriate epistemic shift has been achieved.

Finally, dissemination matters. Publishing in high-impact international journals ensures that critiques of epistemic dominance reach those best positioned to recognise them. Should access be restricted by paywalls, a brief acknowledgement of the irony is sufficient to demonstrate reflexive awareness.

In this way, decolonising global health can be practised as a scholarly orientation that aligns ethical seriousness with professional viability. The goal is not to resolve uncertainty or to determine what works, but to occupy the correct stance toward history and power. When that stance is convincingly performed, the work will speak for itself.

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.