Seeing through the double blind
Randomised controlled trials (RCTs) are an inescapable means of figuring out whether an intervention is efficacious or not. The main tenet behind RCTs is that they should be double-blind, meaning that neither the participants nor the experimenters know who is assuming the real compound and who the placebo. This is certainly the case for drugs supposed to alleviate the symptoms of dementia. These drugs stand on years of development, research, phases of trials, assessment and analysis. The final phase of this research is based on the outcome of cognitive tests. If a treatment proves effective, it finds a place on the shelves. But how can even the ‘gold standard’ of research become tainted, and what role does psychology have to play?
In 2012 research ‘revealed’ that drinking chocolate could be added to the list of treatments for dementia. Chocolate is a good source of flavonoids, naturally occurring compounds that have been associated with a staggering list of health benefits. Desideri and colleagues investigated the effect of flavanol – as administered through ‘dairy-based cocoa drinks’ – on cognitive function in patients at risk of dementia. A double-blind RCT was used. The result was a positive, dose-dependent effect of flavanols on some measures of executive function, all of which was packaged to represent positive changes in cognition.
The popular press were naturally keen to report the excellent news: ‘Chocolate can halt dementia’ was the Daily Express headline of 14 August 2012 (tinyurl.com/nq62j64). It was especially welcome news for Mars Inc., who funded the study and provided the dairy-based cocoa drinks. By capturing a beneficial effect of its product, this company could capitalise on the dementia epidemic.
At the other end of the lifespan, Brain Gym is a controversial, exercise-based intervention designed to improve academic performance in children (see Ritchie et al., 2012, for more). On their website, there is a section headed ‘Why isn’t there more quantitative research?’, which states that they do not use randomised controlled trials (RCTs) to check the programme’s efficacy because ‘most of our instructors are teachers who use [it] in the classroom, they’re working to make a difference for all children, and they question the ethics of not offering equal opportunities to all participants.’
Yet for most psychologists, RCTs are the very epitome of quality research. Should we not be concerned that studies funded by the same industry that creates the product under assessment are perhaps more likely to report positive and larger effect outcomes in its favour than studies carried without such funding?
The ubiquitous bad penny
This potential funding bias might not be a major cause for concern in the case of drinking chocolate. But what about a case where there might be serious implications for treatment or economic consequences for the health service?
We have discovered indications of such potential bias in results for studies assessing donepezil, routinely prescribed as treatment for Alzheimer’s disease (AD). Here, industry-funded, double-blind RCTs that reported the effect of donepezil on cognitive measures revealed, on average, a larger effect of the drug than the independent studies did (Killin et al., 2014). This difference remained after controlling for different study lengths.
Our finding is not a one-off. The bias of funding is the ubiquitous bad penny of pharmaceutical trials and intervention studies, and has been for some time. A 2003 review commented that an estimated 23–28 per cent of biomedical researchers were thought to receive funding from the industry, and 34 per cent of studies published in 1992 in major medical journals had such researchers as lead authors (Bekelman et al., 2003). The consequence of this is apparent: Lundh et al. (2012) reported that clinical trials funded by pharmaceutical companies were more likely to reveal a positive outcome for treatment over placebo than independent trials. In nutritional trials, health effects of non-alcoholic drinks were successfully revealed at a rate of 63 per cent in non-industry intervention studies, which pales in contrast to the 100 per cent success rate purported by industry-funded research (Lesser et al., 2007).
The worst of this bias comes when it is not acknowledged in bodies of evidence like meta-analyses or systematic reviews. When independent and industry-funded studies are amalgamated the combined effect is, at best, slightly altered; at worst, entirely misleading. Cataldo et al. (2010b) teased apart the significant risk factor of tobacco on AD reported by independent studies from the null – even protective – effects reported by the tobacco industry’s research. The contrasting stories that these data provide meant that ‘if one simply combined all 43 studies in a single random effects meta-analysis, one would obtain an inaccurate null result’ (Cataldo et al., 2010b, p.475), implying that tobacco smoke was not a risk factor for AD.
The proof and prevalence of this bias inspires scepticism for any data pushed by a group that could profit from convincing you their product works. This is not restricted to hard health data. Psychological studies consider evidence for a plethora of educational or generic cognitive training interventions, and the chance of funding bias still looms.
A recent case in point is Cogmed, which is a brain-training programme that claims to exploit the plasticity of neural working memory systems to improve learning difficulties associated with attention deficit hyperactivity disorder (ADHD). Recently, it has drawn ire from parents and unimpressed psychologists (see tinyurl.com/p3wja63). These sentiments echoed a lacklustre review that concluded it may, at best, be ‘possibly efficacious’ given that it was often contrasted with poor or inadequate control groups (Chacko et al., 2013). Further criticism came from evidence of its limited effect on general working memory abilities and failure to improve parent-reported ADHD symptoms (Chacko et al., 2014; Chacko et al., 2013). These claims, however, contrast clearly with earlier studies funded by and written by authors with shares in Cogmed (Klingberg, 2012; Klingberg et al., 2005).
Back to Brain Gym: it is worth stressing that the positive data reported may represent vested interests. As laid out plainly by Spaulding et al. (2010), the majority of the evidence detailing Brain Gym’s efficacy was published in either the Brain Gym® Journal or the Brain Gym® Magazine. When assessed formally by means of a systematic review, there was no evidence from peer-reviewed journals to suggest Brain Gym worked, or that these studies had employed sound methods (Hyatt, 2007; Ritchie et al., 2012).
These shortcomings are not specific to Cogmed or Brain Gym, but rather serve as examples of the general attitude towards the brain-training industry. As raised by Owen et al. (2010) and Thompson et al. (2013), brain training produces improvement on the training exercise used in the experiment, but does not result in any statistically significant transfer to other skills.
Cynically, we may not be so surprised. Scientifically, though, we should be puzzled. How does this bias persevere even after studies are put through the wringer of double-blind RCTs? The logic of such trials is that most confounding variables are taken out in the wash, giving clean results. Where does the industry’s stream of good news come from?
Publication and design bias
Plainly, this may simply be another flavour of publication bias. Its prevalence in cognitive sciences has been carefully detailed and reviewed by Ioannidis et al. (2014), who noted that, in spite of a near-even split between negative and positive industry-funded trials investigating the effect of antidepressants, the former are suppressed and unpublished (Turner et al., 2008). In the case that these negative findings might be published, however, we would expect these studies to surface in journals well after positive findings (Misakian & Bero, 1998), affecting the rate at which we update our knowledge.
However, this presupposes that all trials are seen through to the end. It may be more cost-effective to call a poor project to a halt if the initial results are shaky. In this way, publication bias may not explain everything, but design bias may.
Fries and Krishnan (2004) observed in their assessment of American College of Rheumatology meeting abstracts that 100 per cent of the total number of abstracts for RCTs of the study’s sponsor’s drug resulted in a positive outcome. In their discussion, they argue that the ceiling effect seen here could not be attributable to publication bias alone. Instead, they posit that design bias may be the most powerful explanation.
Specifically, as a drug is screened through multiple phases of testing, its weaknesses and strengths are revealed to researchers within the industry. Trials could then be designed to both capitalise on strengths and shade weaknesses. Doing so is a violation of the principle of equipoise, where a drug’s efficacy – in comparison to a control – should always be uncertain, and therefore necessitate research. Djulbegovic et al. (2000) revealed that the pharmaceutical industry violates this principle, whereas independent organisations do not. Coupled with the study’s finding of the industry’s preference to test a product against a placebo or no therapy (as opposed to an active or competing treatment), this suggests that industry studies are designed to be ‘safe’.
Variable of interest
Psychologists need to pay particular attention to the scale or test they use to demonstrate efficacy. This is certainly the case in drug trial literature, as multiple scales can be used to assess one aspect of disease; it would be wrong to assume that these are all equivalent. Indeed, this was the case in trials on donepezil; cognition was assessed by both the Mini Mental State Examination (MMSE) and the Alzheimer’s Disease Assessment Scale-cognitive subscale (ADAS-cog), yet without any clear rationale behind each choice. On the one hand, each scale has its own strengths and weaknesses; but on the other, they broadly assess the same construct. Does the choice of scale really have a bearing on the outcome?
An analysis of available data suggests that it does. We compared ADAS-Cog and MMSE as outcome measures using standardised mean difference (SMD), which allows one to assess outcome when measured with different tools. After separating trials based on their outcome measure, we see that the ADAS-cog is associated with a much greater SMD compared to placebo than the SMD associated with the MMSE, meaning that ADAS-cog shows greater effects of the drug than the MMSE. Both scales ostensibly measure cognition, but clearly not to the same effect.
This difference may be explained by the fact the ADAS-cog has been criticised for being too easy (Cressey, 2012). If this is the case, donepezil participants assessed on this scale may always find themselves close to ceiling level despite exhibiting subtle declines that a different scale would reveal. In other words, donepezil groups may still be declining – just not at a rate the ADAS-cog is designed to detect.
Thus, two scales of cognition, often used interchangeably, and considered equipoise in reviews and meta-analyses, do not necessarily present the same effect. It is noticeable that the drinking chocolate study from Desideri et al. (2012) observed a change in speed in executive tasks, but no difference in the MMSE (which, crucially, assesses neither executive function nor speed). The change in the former is still reported as ‘cognitive function’. Strictly, this is true, but it is disingenuous to use a broad term that could be misinterpreted so as to apply to a wider range of skills. Ultimately, our broad definitions give ample room for researchers to use and choose tasks that are falsely portrayed as equivalent, yet produce different results. The effect of interventions will vary accordingly. Psychologists should be aware of these potential biases.
In spite of careful planning, there is no guarantee that a trial will work. A failed experiment could be an expensive failure, both in terms of time and money. What is your resolve if a three-year, multi-centre trial did not pan out?
If there are enough collected data or possible outcome variables, there is a good opportunity to find or massage the desired effect in spite of what was declared at the outset. Antidepressant trials reviewed by Turner and colleagues (2008) demonstrated that some industry-funded studies failed to find a statistically significant effect on the primary outcome they had specified in the methods they submitted to the US Food and Drug Administration. Instead, a different result was promoted as the significant primary finding, and the original variable of interest was shelved.
Qualitatively, this has been examined in an unsettling historical case analysis from Cataldo et al. (2010a), which investigated correspondence between the tobacco industry and investigators of the Framingham Heart Study. The introduction of Council for Tobacco Research funding to the study came at the cost of the Framingham data, which would later be reinterpreted and reanalysed to conclude that there was no effect of tobacco smoke on coronary heart disease (CHD). Specifically, an analysis of the data stratified by age and ethnicity would suggest some individuals were naturally predisposed to CHD, diverting attention away from the hypothesis that tobacco was a cause. The latter position was pushed by the original investigators and supported by reference to overall mortality data. In the end, the same data produced two contrasting conclusions.
Positive effects produced by the industry may be due to significant methodological shortcomings in spite of using the RCT method. In these cases, reviewers and critics need to identify these issues. The industry, however, has to listen.
A failure to do so became clear when the health benefits of transcendental meditation (TM) programmes were held under scrutiny. Its use pointed towards possible positive effects on mental health and blood pressure. However, a series of meta-analyses reviewed these claims in turn. Firstly, Canter and Ernst (2003) observed a clear divide between studies that claimed a beneficial effect of TM on cognition and those that did not. Specifically, TM’s success was linked to inadequate control groups (echoing the findings of Chacko et al., 2013 and Djulbegovic et al., 2000). On TM’s link with blood pressure, Canter and Ernst (2004) argued that, in a field saturated by TM-affiliated studies, even the most stringent RCT failed to adequately assess baseline measures and also account for differences between experimental groups, such as rates of medication. This was raised as a serious criticism and a source of bias in the TM literature.
After these criticisms were published, Anderson et al. (2008) produced an updated meta-analysis of TM and blood pressure. This naturally contained the criticised studies analysed by Canter and Ernst four years previously. The authors plainly concluded that the quality of TM studies varied. However, given this range of quality their approach was to highlight the high-quality studies, and ignore the fundamental problems raised by Canter and Ernst. The authors nonetheless concluded that TM was responsible for clinically meaningful changes in systolic and diastolic blood pressure. Unlike previous meta-analyses, this was funded by an unlimited gift from Dr Howard Settle (see Acknowledgements in Anderson, 2008), who is responsible for personally funding the construction of TM centres in North America (see tinyurl.com/lck2qfm).
So, how do we get to the truth of a product’s effectiveness? We may be starting on a poor footing. Psychology is fraught with biases and possible confounding effects. For instance, even well-established phenomena in short-term memory – such as the phonological similarity or word-length effects – are affected by the strategies participants use (Logie et al., 1996). How many other possible variables could explain a part of a human’s cognition or behaviour? What if participants are anxious or if they are not familiar with the words we ask them to remember? At what point do we stop controlling for these variables?
We cannot – and do not – address all confounds. Instead, we control for the bigger, broader variables like age, education or gender and work on the assumption that multiple measurements merge and overlap to reveal some identifiable construct or mechanism that can be generalised (Lilienfeld, 2012), and rely on replications (see tinyurl.com/psycho0512) to make sure our finding is not restricted to one place and time (as Manzi, 2010, would argue). The least we can do, in addition, is to control for industry bias, especially if it is something that ‘researchers cannot stop’ (Seife, 2012, p.63).
Such control has started to take place in Europe. This year, MEPs voted in favour of the Clinical Trials Regulation, which was created to ensure that trials are pre-registered before they are run, and that the results are clearly reported and explained in lay terms within a year of the study’s end. This takes away the likelihood of publication bias, design bias and post-hoc massaging as detailed earlier. Pre-registration may prove an effective tool also in cognitive science (Chambers, 2013; see discussion in The Psychologist, July 2013).
However, the scientific community cannot coast along on the new regulation alone. Researchers will still need to be relentlessly critical of industry-funded research. The ammunition closest to hand for a psychologist would be their knowledge of statistics and experimental design, but an education in psychometrics can define the overlap between an affected construct and the test used to assess it, cross-examining the exact claim of industry-funded studies.
Psychologists are also in a position to take on the industry with their own research. This year marks the 50th anniversary of the 1964 Surgeon General’s Report on Smoking and Health. To commemorate this event, the role of psychologists in the continued campaign for tobacco control was reviewed recently (DeAngelis, 2014). Amongst other contributions, psychologists were responsible for developing population-wide smoking cessation interventions, such as telephone quitting lines, which are readily available as government-funded amenities across the United States. Furthermore, related psychological interventions have been carefully developed to be sensitive to different populations so as to identify the exact relationships between groups and outcomes associated with their smoking. These efforts stand in contrast to the evidence surrounding nicotine patches, which is a generic treatment with an efficacy affected by industry-funding (Etter et al., 2007).
Funding sources will continue to bias scientific research. The move towards trial registration will take the spin off industry-funded research, but there is still a need for diligence. As this bias perseveres, researchers need to remain critical and forge a way around the bias or, at least, flag it at every instance.
- Lewis Killin is in the Department of Psychology, University of Edinburgh
- Sergio Della Sala is in the Department of Psychology, University of Edinburgh
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