Category Archives: Politics

From my point of view, this is big “P” politics of Nation States or Provinces within Nation States.

Global heating isn’t important–if you’re not suffering.

In the last weeks of June, Europe experienced a heatwave that broke temperature records from France through to Hungary. The heatwave combined high daytime and nighttime temperatures with high humidity. The result was more than 2,000 excess deaths in France alone.

The third heatwave of the European summer has started.

I have been fascinated by the political and technocratic response to the heatwave because, rhetorically at least, this summer has broken through the background hum of climate change conversations. There is a sense of urgency that I have not heard before. “Panic” is probably too strong a word, but governments are clearly worried. Will Europe be liveable in summer in 10 years time?

Having grown up with hot Australian summers and no air conditioning, I was familiar with the routine. Windows open at night to cool the house. Curtains and windows closed during the day to prevent it heating up. Fans helped. Evaporative cooling only worked if the humidity was not already too high. If it was too high, it didn’t feel like you were cooling, it felt like a sauna.

Where I now live in Europe, domestic air conditioning is not permitted, and the Australian strategies only worked partially in my apartment. Before the heatwave began, the internal wall temperatures were in the low 20s, by the end of the heatwave they were around 28.5. The thermal mass of the building had increased. The concrete and steel had absorbed the rolling heat of the day and radiated it out at night. Sleep was late in coming, patchy, and uncomfortable.

The thermal mass problem tracked something a colleague of mine at icddr,b and I had found in slums in Dhaka, Bangladesh. We had placed temperature data loggers in people’s dwelling and captured the rise and fall of temperature and humidity during the day and night. The construction materials were essentially tin and concrete. A tin roof and tin walls became an oven during the day, but cooled rapidly at night (low thermal mass). A concrete roof and concrete walls (high thermal mass) meant that the building’s internal temperature didn’t rise rapidly during the day, but nor did it cool rapidly at night. The concrete smoothed out the temperature variations, but in the absence of active cooling, it eventually rose to the average ambient temperature.

This is the challenge that Europe faces in a world of much hotter summers. Standard passive cooling techniques will get you only so far. Shade to avoid the direct rays of the sun or solar reflectance (albedo) surface to avoid the impact of direct exposure helps. High emissivity surfaces that radiate heat outwards in the cool of the night. Insulation (thermal resistance) to prevent the heat penetrating. Evaporative cooling if humidity permits and water is available.

In summers of regular heatwaves, however, these techniques are limited. Passive cooling can delay equilibrium, but it cannot overcome it. Eventually the thermal properties of the buildings catch-up. And it is difficult to design the building that sheds heat and never captures heat for a scorching summer, but retains and doesn’t lose heat in the winter. All of this assumes that there is even an option to make massive design changes. The vast majority of European housing stock was built with winters in mind, not summers. The oldest buildings, those that give the historic beauty to European cities, have poor thermal properties, and structural changes to them are heavily restricted by conservation laws.

If one cannot rely on passive cooling, then active cooling becomes the fallback. Historically, there have been very low rates of air conditioning in Europe compared to the United States. The latest heat wave, however, has opened discussion about allowing those in “genuine need” to install air conditioning. This, in itself, opens a can of worms. Who has genuine need? Who will pay for the active cooling for those who need it but cannot afford it. The elderly and those with chronic health conditions are often most vulnerable to heat stress. As groups of people, however, they tend to have less disposable income for the purchase and installation of active cooling. Unfortunately, in a continuous heat-stressed environment, everyone will be in need of cooling.

Widespread European air conditioning will also carry at least two unintended consequences. The first is that air conditioning needs manufacturing and maintaining, and power to run it. This will inevitably have greenhouse gas-production issues for a world that desperately needs to reduce greenhouse gas emissions. The second is that, if one is cooling the inside of a building, one is inevitably dumping heat into the outside. And it is slightly worse than that, you cannot move heat from inside to outside a building cost free, you must generate some additional heat to do that. Large scale air conditioning in cities can raise the external air temperature between 1 and 2 degrees, and it creates a feedback loop, because additional internal cooling is needed to overcome the increase in the rising external heat. The consequence for those who do not have air conditioning (those without “genuine need” or those without homes) is that they will experience even more extreme heat waves so that others may suffer less.

Will Europe be liveable in the summers in 10 years time? It really depends on what you mean by “liveable”. The dead trees I have seen– already unable to survive a June heatwave–do not augur well (see the related article on an iconic English oak tree). Passive cooling will help, but as the thermal mass argument demonstrates, it will be insufficient–the second law of thermodynamics prevents it. The answer Europeans seem to be reaching for is air conditioning–for those who can afford it. The heat it dumps outside falls on those who cannot, just as the emissions it produces fall on everyone, everywhere, including places already less able to cope. Widespread air conditioning does not solve Europe’s heat problem. Change nothing about how we live, and shift the cost onto those with the least capacity to bear it.

 

 

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.

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.