All that glisters… How to assess the ‘value’ of a scientific paper

Abstract

Doctors are expected to keep up to date with the literature, and to change their practice on the basis of what they have read. We believe that the skills needed for evaluating and interpreting scientific papers are often lacking. Even when they are taught, the emphasis is often focused on technical aspects of a paper without consideration of its value, a term we use here to encompass not only the quality of a paper's methods, but also its context and importance. We argue that critical appraisal, the term used to describe the assessment of a paper's methodological niceties [1], should never take place in isolation but must always occur in parallel with assessment of its value, since a paper may be methodologically sound but contribute little to a better understanding of the subject. Here, we discuss various aspects of scientific papers that contribute to or detract from their value, and suggest a stepwise approach for assessing them. The purpose of a scientific publication, of which there are numerous types, is to communicate information. Editorials are summary or personal views, perhaps commenting on a specific paper. Reviews are longer, in-depth analyses of the literature; they are most persuasive when their analysis is objective but their conclusions (as with editorials) are often subjective and personal. Specific forms of supposedly objective reviews are quantitative or systematic reviews, or meta-analyses[2]. Case reports describe one (or more) specific clinical cases, either so unusual as to be of interest, or from which it is hoped some particular lesson can be learned. A letter (correspondence) is a comment on, or criticism of, another's published paper, or seeks answers to a question. A letter may also convey information or data that do not constitute a full study but nonetheless are thought worthy of dissemination. Finally, there are experimental investigations. Broadly, these attempt to answer a question by the use of the ‘scientific method’, which involves the following process [3, 4]. First, the researcher formulates a hypothesis. This hypothesis may represent current ideology (the current theory, or paradigm), or it may be an idea developed de novo (e.g. suggested by preliminary observations). The hypothesis leads to an experimental prediction: if a certain experiment is conducted, then this predicted result should obtain if the hypothesis is correct. A result consistent with the prediction supports the hypothesis, but does not ‘prove’ it (thus scientific proof is very different from mathematical proof). If, on the other hand, the experimental result is not as was predicted, then either the hypothesis is incorrect (so disproved) or the conduct of the experiment was flawed. There are many types of experimental investigations: clinical studies or trials (the terms are often used interchangeably, although the latter is sometimes restricted to investigations of a treatment's efficacy); laboratory investigations; mathematical modelling of data; and some observational studies and audits. We focus here on experimental investigations since these are the papers that advance the knowledge base the most. There are generally two aspects to excellence in an experimental study: first, the study's conduct (of which handling of the data is an inherent part), and second, its presentation. Important aspects of presentation are covered by journals' instructions to authors and by specific publications [5, 6], and we will not discuss these in detail here. First, the study must consider a clear hypothesis that is stated unambiguously, ideally, illustrated by the results that would be expected if the hypothesis were true. The final results and conclusion of the study should relate to this prediction and must either refute or be consistent with the hypothesis. Second, the study must have appropriate ethical approval (or conform to animal research guidelines). We will not consider this issue further, since it has been addressed recently [7]. Third, the technical conduct of the experiment must be sound. Particular attention should be given to the avoidance of surrogate measures, appropriate measurement tools, proper randomisation and blinding, appropriate use of control groups, and appropriate application and interpretation of statistics. We consider each of these below. Surrogate measures or end-points have serious limitations. For example, a study of the control of minute ventilation may not actually involve measurement of this outcome at all, but instead may try to derive conclusions based on the measurement of another, related variable (say, arterial Pco2). The problem is that other factors may influence the related variable (e.g. ventilation is not the only factor influencing Pco2). Furthermore, measures that seem superficially related may not be; for example, although flecainide reduces cardiac arrhythmias, it increases mortality – a much more relevant end-point [8]. Surrogate measures are sometimes used in clinical studies because of the difficulty in measuring the desirable end-point, such as long-term survival. They might also give crude estimates of trends over time for certain variables [9], but they have very little (if any) place in studies that seek to question or overturn fundamental hypotheses in the underlying science. Measuring devices and assessment tools must be valid (measure what they are supposed to measure), accurate (measure the true quantity), and reliable (different users obtaining the same results) – aspects that often escape attention in manuscripts. This is not restricted to technical measurements; for example, assessment of ‘maternal satisfaction’ with the use of a simple visual analogue scale continues widely despite little evidence to support it [10]. When technology is used, coefficients of variation should be given, but rarely are. Further, there ought to be some confidence as to how the technology works. For example, much of the growing literature on the bispectral index (BIS) as a monitor of ‘awareness’ raises concerns. Since it is not known precisely what is being measured by the BIS [11], it can never be known whether an unexpected result has arisen because the BIS is invalid or inaccurate, or because the hypothesis being tested is incorrect [12]. Randomisation and blinding are intended to minimise the influence of bias. The hope with randomisation is that all ‘confounding factors’ (both known and unknown) that might influence the outcome will be distributed equally amongst the groups. If any differences are found they can therefore be attributed to the sole factor – the treatment under study – that has not been ‘shared out’ in this way. However, even with proper randomisation, groups may be unequal: chance alone might result in one group's subjects being older, heavier, younger or just luckier than those in the other group. Even when groups appear equal, small inequalities might combine to influence the results. For example, in a study by Greif et al. [13] into the possible anti-infective effect of peri-operative oxygen therapy, patients randomly allocated to receive extra oxygen were by chance more likely to be fitter and less likely to be smokers, to have inflammatory bowel disease, and to undergo rectal surgery than those in the ‘no oxygen’ group. Could these factors have combined to contribute to the dramatic reduction in infection seen in the ‘oxygen’ group, such that a subsequent study obtained completely the opposite results [14]? In addition, the human urge to guess or manipulate treatment allocations, or otherwise interfere with proper randomisation in studies, is well reported [15]. Blinding is present when the person treating the patient, or making the assessments, does not know which patients receive which treatment. Some studies fail to take even the simplest steps to ensure blinding, while others go to extraordinary lengths (for an example of the latter, see Smith and Thwaites's [16] commendable study comparing intravenous with inhalational anaesthesia). Occasionally, blinding is impossible (e.g. when comparing two different laryngoscope blades or bougies [17]), but the results of a blinded study are always more persuasive. Indeed, studies with insufficient blinding tend to report greater treatment effects than those with proper blinding procedures [15]. Control groups may be inappropriate because of poor randomisation or blinding. Even if these are sound, though, there may be other reasons why treatment effects may be masked or exaggerated by problems with control groups: lack of consideration of other possible ‘confounding factors’; use of historical, rather than contemporaneous, controls; comparison of a treatment against placebo instead of standard practice, or against an inappropriate treatment; or (at worst) lack of a control group at all. Much of the above might give the impression that the testing of hypotheses by close attention to the study's conduct will always give a clear-cut result. Unfortunately, this is not the case, because we can never achieve certainty; the best we can do is use statistical analysis to indicate the degree of uncertainty [18]. A full discussion of statistical methods is dealt with elsewhere [19], and here we consider only two related areas that commonly cause difficulties: significance and power. Significance. If, in a study, one drug appears more effective than another, the traditional approach is to ask the question: ‘What is the likelihood (or probability) that this result is a chance finding, and that these two drugs are in fact equivalent?’ This approach (testing the equivalence, as opposed to testing the difference) is known as testing the null hypothesis. It is important to stress that this null hypothesis assessed by the statistical test may not always be exactly the same as the underlying scientific hypothesis being examined by the study as a whole: the result of the former will help interpret the latter. Many statistical tests ultimately generate a ‘p-value’: the lower the p-value, the less likely it is that the null hypothesis is correct. A p-value of 0.03 indicates that if the two drugs are indeed equivalent, chance alone would be expected to yield the observed results three out of every 100 times one conducted the study. Conventionally, a p-value of < 0.05 is taken to represent ‘statistical significance’, although this value can and should be adjusted in certain circumstances, for example if multiple comparisons are made [20, 21]. Confidence intervals can be used as an alternative to testing the null hypothesis [22, 23]; nonetheless, the conclusions reached by using confidence intervals are invariably the same. The real problem lies in how p-values are interpreted rather than how they are calculated [24]. An entirely different approach is to interpret a study's results mathematically in the context of prior knowledge (Bayesian statistics) [25, 26]. Regardless of the method of calculating or presenting statistical significance, the smaller the p-value, or the further away from zero the difference in confidence intervals, the less likely the result is to be a ‘chance’ finding and therefore the more likely it is that the difference between the two groups is indeed ‘genuine’. But such a chance finding is still possible, albeit unlikely; as Counsell et al. [27] point out, chance ‘…doesn’t get the credit it deserves'. Furthermore, a low p-value does not exclude poor methodology in the conduct of the study. Power. If the p-value in a drug study is, say, 0.07, does this mean there is genuinely no difference between the two drugs? Or does it mean that there might be a true difference, but that the study has simply failed to show it? It is specifically to help answer such questions that a power analysis is useful. The power analysis estimates how likely it is that a negative result can be ‘believed’. One emerging problem is that some researchers (or their critics) are placing far too much emphasis upon power analysis [28]. One example demonstrates the type of misplaced faith in power analysis: ‘…at least 400 patients would be required to prove there is no statistically significant difference between the groups…’[29] (our emphasis). Such statements reveal a poor understanding of the scientific method and of the concept of scientific proof. One reason for our concern is that the concept of power analysis itself has very serious limitations. Power analyses are only crude estimates of a sample size (indeed, the word ‘crude’ is emphasised by statisticians [30]). For example, two main elements that contribute to power for normally distributed continuous data are the difference between the means that is deemed important and the expected standard deviation (SD) of the measure of interest. Both of these are subject to serious shortcomings. The choice of what constitutes an ‘important difference’ is almost entirely subjective, and small but arbitrary adjustments to its value can have a great impact upon a study's calculated power. Where no previous data exist, the expected SD is usually taken from a pilot study, often without a control group, and by definition always smaller and less robust than the planned substantive study. In reality, the power analysis itself is probably best expressed in terms of a confidence interval: for example, ‘Power analysis indicated that we would require 20–60 subjects to be 70–90% confident of detecting a difference between the means of 10–50 s’– although this is rarely done. The crudeness of the power analysis as a tool is reflected in the different sample sizes yielded by different methods. If we assume that for a hypothetical study, the important difference is 1.0 arbitrary units, with a standard deviation of 0.8 arbitrary units, then various calculations give a sample size per group (with 80% power at p < 0.05) of 10 [30], 11 [31], 13 [32] and 18 [33]. So at best, power analysis only gives an approximate estimate of sample size. Indeed, Bacchetti [34] has suggested that a study's power should only be criticised if the study has no other shortcomings; in other words, all other features of a study (especially relating to its conduct) are far more important than its power analysis. In practice, the actual sample sizes of studies are related to the type of outcome, the variability of the result and the statistical test used. We observe that in published studies, sample sizes tend to fall into three groups, though with considerable overlap in which the outcome is and or there is little variability with factors (e.g. laboratory or studies in which experimental can be with use smaller sample usually increases patients are since are to studies comparing have sample in which the outcome is variability is great factors are much sample sizes It is how often studies and their sample sizes fall into these groups. 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