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Twenty top tips for interpreting scientific claims

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Posted November 21, 2013

Aiming to improve policy-makers’ understanding of the imperfect nature of science, academics from the Universities of Cambridge and Melbourne have created a list of concepts that they believe should be part of the education of civil servants, politicians, policy advisers and journalists

 

Science is not just a body of facts – it’s important to have a grasp of the process by which conclusions are drawn, and the possible pitfalls on that path

 

Professor David Spiegelhalter

Scientists from the UK and Australia, concerned with the lack of scientific knowledge amongst key decision makers, have created 20 concepts to help those who interact regularly with science and scientists.

Recent issues such as nuclear power, bee declines, and the role of badgers in bovine tuberculosis have seen fierce debates and policy decisions being made without the support of the scientific community, something Professors William Sutherland, David Spiegelhalter and Mark Burgman have set out to change.

These scientists want to help people grasp the “imperfect nature of science” and enable policy-makers to interrogate their advisers and experts instead of simply accepting information as it is given. Though change will take time, it is their belief that “a wider understanding of these 20 concepts by society would be a marked step forward”, and could only lead to a better-informed future.

Professor Spiegelhalter said “These tips could be used as a checklist when confronted with scientific claims.  Science is not just a body of facts – it’s important to have a grasp of the process by which conclusions are drawn, and the possible pitfalls on that path”

There is an obvious need to make sure that scientific policy is based on a sound understanding of science; this means making sure that policy-makers know the right things to ask, and how to interpret the answers they get. There have been many suggestions of how to increase the level of scientific knowledge in the political community, from encouraging more scientists to become politicians, to expanding the role of chief scientific advisors. However, none of these solutions fully address the fundamental issue of widespread “scientific ignorance” amongst those who have the ability to vote in parliament.

The homogeneity of policy makers’ backgrounds shows just how far-reaching this problem is. No member of the current British cabinet has a scientific degree – the closest is Vince Cable, who initially read Natural Sciences at Cambridge before switching to Economics. Six cabinet members read Politics, Philosophy and Economics (PPE) at Oxford, including Ed Davey MP, the Secretary of State for Energy and Climate change. Of Britain’s 650 members of parliament, only Cambridgeshire MP Julian Huppert is a scientist; David Willets MP, the Minister of State for Universities and Science, read PPE.

This list of concepts will teach skills closely related to those that politicians already have, and will help people “understand the quality, limitations and biases of evidence”. This will, in turn, allow better interrogation of those communicating scientific information. By explaining the scientific process, these academics have helped to demystify science and make it accessible to those creating the country’s scientific policy. It is not a question of turning every policy-maker into a scientist, but of arming them with the tools to understand and question the scientific information they receive.

Some of the concepts seem common sense (“Scientists are human”), others less so (“Regression to the mean can mislead”, “Beware the base rate fallacy”).  All contain practical advice and recommendations that, if followed, should help policy-makers better interact with science and scientists and understand the limitations of evidence. Though the authors acknowledge that improvements in policy will not happen instantaneously, and that uncertainty is inherent in the scientific method, they nonetheless feel that these concepts are the first step to take if we are to more closely integrate science into political decision-making.

Click here to read the Nature article.


The list in full

Differences and chance cause variation. The real world varies unpredictably. Science is mostly about discovering what causes the patterns we see. Why is it hotter this decade than last? Why are there more birds in some areas than others? There are many explanations for such trends, so the main challenge of research is teasing apart the importance of the process of interest (for example, the effect of climate change on bird populations) from the innumerable other sources of variation (from widespread changes, such as agricultural intensification and spread of invasive species, to local-scale processes, such as the chance events that determine births and deaths).

No measurement is exact. Practically all measurements have some error. If the measurement process were repeated, one might record a different result. In some cases, the measurement error might be large compared with real differences. Thus, if you are told that the economy grew by 0.13% last month, there is a moderate chance that it may actually have shrunk. Results should be presented with a precision that is appropriate for the associated error, to avoid implying an unjustified degree of accuracy.

Bias is rife. Experimental design or measuring devices may produce atypical results in a given direction. For example, determining voting behaviour by asking people on the street, at home or through the Internet will sample different proportions of the population, and all may give different results. Because studies that report ‘statistically significant’ results are more likely to be written up and published, the scientific literature tends to give an exaggerated picture of the magnitude of problems or the effectiveness of solutions. An experiment might be biased by expectations: participants provided with a treatment might assume that they will experience a difference and so might behave differently or report an effect. Researchers collecting the results can be influenced by knowing who received treatment. The ideal experiment is double-blind: neither the participants nor those collecting the data know who received what. This might be straightforward in drug trials, but it is impossible for many social studies. Confirmation bias arises when scientists find evidence for a favoured theory and then become insufficiently critical of their own results, or cease searching for contrary evidence.

Bigger is usually better for sample size. The average taken from a large number of observations will usually be more informative than the average taken from a smaller number of observations. That is, as we accumulate evidence, our knowledge improves. This is especially important when studies are clouded by substantial amounts of natural variation and measurement error. Thus, the effectiveness of a drug treatment will vary naturally between subjects. Its average efficacy can be more reliably and accurately estimated from a trial with tens of thousands of participants than from one with hundreds.

Correlation does not imply causation. It is tempting to assume that one pattern causes another. However, the correlation might be coincidental, or it might be a result of both patterns being caused by a third factor — a ‘confounding’ or ‘lurking’ variable. For example, ecologists at one time believed that poisonous algae were killing fish in estuaries; it turned out that the algae grew where fish died. The algae did not cause the deaths.

Regression to the mean can mislead. Extreme patterns in data are likely to be, at least in part, anomalies attributable to chance or error. The next count is likely to be less extreme. For example, if speed cameras are placed where there has been a spate of accidents, any reduction in the accident rate cannot be attributed to the camera; a reduction would probably have happened anyway.

Extrapolating beyond the data is risky. Patterns found within a given range do not necessarily apply outside that range. Thus, it is very difficult to predict the response of ecological systems to climate change, when the rate of change is faster than has been experienced in the evolutionary history of existing species, and when the weather extremes may be entirely new.

Beware the base-rate fallacy. The ability of an imperfect test to identify a condition depends upon the likelihood of that condition occurring (the base rate). For example, a person might have a blood test that is ‘99% accurate’ for a rare disease and test positive, yet they might be unlikely to have the disease. If 10,001 people have the test, of whom just one has the disease, that person will almost certainly have a positive test, but so too will a further 100 people (1%) even though they do not have the disease. This type of calculation is valuable when considering any screening procedure, say for terrorists at airports.

Controls are important. A control group is dealt with in exactly the same way as the experimental group, except that the treatment is not applied. Without a control, it is difficult to determine whether a given treatment really had an effect. The control helps researchers to be reasonably sure that there are no confounding variables affecting the results. Sometimes people in trials report positive outcomes because of the context or the person providing the treatment, or even the colour of a tablet. This underlies the importance of comparing outcomes with a control, such as a tablet without the active ingredient (a placebo).

Randomization avoids bias. Experiments should, wherever possible, allocate individuals or groups to interventions randomly. Comparing the educational achievement of children whose parents adopt a health programme with that of children of parents who do not is likely to suffer from bias (for example, better-educated families might be more likely to join the programme). A well-designed experiment would randomly select some parents to receive the programme while others do not.

Seek replication, not pseudoreplication. Results consistent across many studies, replicated on independent populations, are more likely to be solid. The results of several such experiments may be combined in a systematic review or a meta-analysis to provide an overarching view of the topic with potentially much greater statistical power than any of the individual studies. Applying an intervention to several individuals in a group, say to a class of children, might be misleading because the children will have many features in common other than the intervention. The researchers might make the mistake of ‘pseudoreplication’ if they generalize from these children to a wider population that does not share the same commonalities. Pseudoreplication leads to unwarranted faith in the results. Pseudoreplication of studies on the abundance of cod in the Grand Banks in Newfoundland, Canada, for example, contributed to the collapse of what was once the largest cod fishery in the world.

Scientists are human. Scientists have a vested interest in promoting their work, often for status and further research funding, although sometimes for direct financial gain. This can lead to selective reporting of results and occasionally, exaggeration. Peer review is not infallible: journal editors might favour positive findings and newsworthiness. Multiple, independent sources of evidence and replication are much more convincing.

Significance is significant. Expressed as P, statistical significance is a measure of how likely a result is to occur by chance. Thus P = 0.01 means there is a 1-in-100 probability that what looks like an effect of the treatment could have occurred randomly, and in truth there was no effect at all. Typically, scientists report results as significant when the P-value of the test is less than 0.05 (1 in 20).

Separate no effect from non-significance. The lack of a statistically significant result (say a P-value > 0.05) does not mean that there was no underlying effect: it means that no effect was detected. A small study may not have the power to detect a real difference. For example, tests of cotton and potato crops that were genetically modified to produce a toxin to protect them from damaging insects suggested that there were no adverse effects on beneficial insects such as pollinators. Yet none of the experiments had large enough sample sizes to detect impacts on beneficial species had there been any.

Effect size matters. Small responses are less likely to be detected. A study with many replicates might result in a statistically significant result but have a small effect size (and so, perhaps, be unimportant). The importance of an effect size is a biological, physical or social question, and not a statistical one. In the 1990s, the editor of the US journal Epidemiology asked authors to stop using statistical significance in submitted manuscripts because authors were routinely misinterpreting the meaning of significance tests, resulting in ineffective or misguided recommendations for public-health policy.

Study relevance limits generalisations. The relevance of a study depends on how much the conditions under which it is done resemble the conditions of the issue under consideration. For example, there are limits to the generalizations that one can make from animal or laboratory experiments to humans.

Feelings influence risk perception. Broadly, risk can be thought of as the likelihood of an event occurring in some time frame, multiplied by the consequences should the event occur. People’s risk perception is influenced disproportionately by many things, including the rarity of the event, how much control they believe they have, the adverseness of the outcomes, and whether the risk is voluntarily or not. For example, people in the United States underestimate the risks associated with having a handgun at home by 100-fold, and overestimate the risks of living close to a nuclear reactor by 10-fold.

Dependencies change the risks. It is possible to calculate the consequences of individual events, such as an extreme tide, heavy rainfall and key workers being absent. However, if the events are interrelated, (for example a storm causes a high tide, or heavy rain prevents workers from accessing the site) then the probability of their co-occurrence is much higher than might be expected. The assurance by credit-rating agencies that groups of subprime mortgages had an exceedingly low risk of defaulting together was a major element in the 2008 collapse of the credit markets.

Data can be dredged or cherry picked. Evidence can be arranged to support one point of view. To interpret an apparent association between consumption of yoghurt during pregnancy and subsequent asthma in offspring, one would need to know whether the authors set out to test this sole hypothesis, or happened across this finding in a huge data set. By contrast, the evidence for the Higgs boson specifically accounted for how hard researchers had to look for it — the ‘look-elsewhere effect’. The question to ask is: ‘What am I not being told?’

Extreme measurements may mislead. Any collation of measures (the effectiveness of a given school, say) will show variability owing to differences in innate ability (teacher competence), plus sampling (children might by chance be an atypical sample with complications), plus bias (the school might be in an area where people are unusually unhealthy), plus measurement error (outcomes might be measured in different ways for different schools). However, the resulting variation is typically interpreted only as differences in innate ability, ignoring the other sources. This becomes problematic with statements describing an extreme outcome (‘the pass rate doubled’) or comparing the magnitude of the extreme with the mean (‘the pass rate in school x is three times the national average’) or the range (‘there is an x-fold difference between the highest- and lowest-performing schools’). League tables, in particular, are rarely reliable summaries of performance.

 

Source: Cambridge University

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