Focus on Alternative and Complementary Therapies
www.pharmpress.com/fact
Focus Alternat Complement Ther©2005 Pharmaceutical Press
Focus Altern Complement Ther 2006; 11: 96–100
Placebo is perhaps the single most important key to understanding both evidence-based and patient-oriented medicine. This is especially true for alternative, complementary and integrative medicine, where belief systems and mind–body interactions are paramount. As control comparisons in clinical trials, placebo pills and sham procedures are the standard against which most treatments are judged.1–4 In a broader sense, the term ‘placebo’ has been used when describing health effects resulting from interventions as disparate as varied pill colour,5 doctors’ advice,6–8 psychotherapy,9 expectancy,10,11 suggestion12 and classical conditioning.13 Indeed, concepts and procedures relating to placebo permeate nearly all of medical theory and practice. This essay argues that the many facets of placebo are inter-related, if not entirely consistent, and that together they point towards healing pathways of great potential importance. Arguments here also provide the rationale for large, publicly funded pragmatic trials that include unblinded and no-treatment groups.
For more comprehensive reviews of placebo, I refer readers to the works by Guess et al,14 Harrington,15 Kirsch,16 Moerman17 and Shapiro & Shapiro.18 Because the strongest data regarding placebo effects arise from investigations of pain and depression, the reader is also referred to works by Benedetti et al,19 Hoffman et al,20 Andrews21 and Walsh et al.22 Sceptical perspectives have been championed by Hrobjartsson & Gotzsche23 and Kienle & Kiene.24 An article by Walach in the June 2003 issue of FACT25 and a review article we recently wrote26 might also be useful. The purpose of the current essay is not to review the evidence on placebo effects, but to work through and rethink how this evidence should guide research and clinical practice.
Following Moerman27–30 and Kaptchuk,31 I attribute health-related changes following sham interventions not to the interventions themselves but to awareness and received meaning within the recipient. If placebo pills or sham interventions are inert, they by definition can have no effect. Hence if placebo effects occur, as they most certainly do, they come not from the sham inert interventions themselves but from perception, reaction or interpretation on the part of the recipient, and from learned (and perhaps innate) response patterns. A great deal of evidence suggests that placebo effects, perhaps better referred to as meaning effects, are real and often substantial. These phenomena should therefore be better accounted for in the design, interpretation and application of clinical research.
While some medical historians trace the origins of the RCT back to the 19th century,32–34 it was not until the 1940s and 1950s that the double-blind randomised trial (dbRCT) took its place as the cornerstone for evaluation of medical interventions.35–37 Along with the dbRCT came the placebo. Randomisation to blinded placebo seemed the perfect method to control for five potentially important sources of bias: (i) variability in natural course of disease, (ii) regression to the mean, (iii) sampling biases, (iv) participant/subject error/bias and (v) physician/scientist/evaluator error/bias. Early proponents of dbRCTs, such as Beecher, argued that placebo effects were often ‘powerful’38 and hence needed to be accounted for in the rational evaluation of medical treatments. Implicitly, placebo effects tended to be equated with participant/subject bias. The idea that placebo responses were due to awareness and received meaning within the subject was not lost on Beecher: ‘However inert a placebo may be in the usual sense, it is not inert in its effect. It is a powerful agent whose primary site of action is the cerebral cortex. There is a great deal of evidence that the significance of a stimulus determines whether or not it will evoke a sensation.’39
Herein lies the paradox, the challenge and the opportunity. Conventional dbRCTs include concealed allocation so study participants (and their evaluators) are unaware of whether they are randomised to treatment or placebo. This limits their ability to prejudice reporting (and subsequent data entry, coding, analysis and interpretation). But if awareness and received meaning can exert powerful effects, then something is indeed lost whenever we extrapolate from blinded trials to actual practice. Observed differences between allocation–concealed active and placebo groups (i.e. specific effects) cannot be generalised to actual practice (i.e. ‘the real world’), where people are usually quite aware of which treatment they are taking. Such ‘general effects’ could perhaps be generalised from RCTs comparing no treatment and/or blinded treatment to unblinded open-label treatment, but that would introduce unwanted bias. Or would it?
Perhaps we need to be more careful about identifying specific potential biases and limitations. By most accounts, randomisation of sufficient numbers of participants to alternative groups adequately controls for natural variability in disease course, regression to the mean and baseline differences due to sampling. That leaves the biases introduced by participants and evaluators. At the risk of being labelled a heretic, I would argue that in most cases an effect resulting from a participant’s awareness of treatment should not be considered a bias but instead should be interpreted as a real and potentially important health effect. Let me explain. Medical interventions are designed to extend life and/or to improve quality of life, including both symptoms (pain, nausea, itching, sadness) and functions (walking, talking, interacting with others, activities of daily living). While there is some consensus regarding the goal and measurement of life extension (and avoidance of major events such as heart attacks, strokes and hospitalisations), the evaluation of interventions designed to impact on quality of life is more problematic. Impacted domains vary in value among persons. For example, one person may detest itching but not be bothered much by nausea, while another may have an opposing viewpoint. A second problem results when study participants knowingly or unknowingly rate their health states as higher or lower depending on their knowledge and attitudes regarding the treatment being studied.
Doctors, lawyers, legislators, judges and juries have all agreed that the benefits of a medical intervention should be judged according to the values of the recipient, not the provider. For example, when making difficult end-of-life decisions, doctors and family members are admonished to consider the patient’s individual values, not their own. Nevertheless, clinical research design and interpretation appear to be directed more by scientific than lay values. Conventional RCTs seek to blind patients from knowledge of whether or not they are receiving treatment with the justification that patients’ perception and reporting of their own health may introduce bias. However, it is the patient’s own perception and valuing of symptoms and functions that provides the rationale for health research and intervention in the first place! While measurement and interpretation of outcomes such as mortality, heart attacks and hospitalisations is fairly straightforward, the same is not true for day-to-day health-related quality of life, which, it turns out, is the object of most medical therapies. The argument that blinding is necessary to control for patients’ subjectivities flies in the face of the very purpose of most treatments – to modify and improve those subjectivities!
It seems to me that by insisting on only fully blinded trials, we may be throwing out the baby with the bath-water. After all, it is patient-assessed benefits that we are aiming to quantify and predict. If patient-assessed benefits are influenced by awareness of treatment and we are interested in evaluating patient-assessed benefits, ergo, we must assess these benefits under conditions of awareness of treatment. By ignoring, deriding or minimising so-called placebo effects, and by focusing almost exclusively on blinded treatments vs. blinded placebos, we may greatly bias our estimates of real-world effects. It also seems to me that we are, perhaps unconsciously, judging effects with physician–scientist values, not with the values of the people for whom the treatments are intended. Medical scientists try very hard to reduce bias, and are very interested in mechanisms of action. Patients, on the other hand, seek to alleviate symptoms and improve functions, and are much less concerned with mechanism and potential bias.
I am not advocating that we give up on the idea of allocation concealment, far from it. I am actually so concerned with the potential biases introduced by the interested parties who conduct trials that I think that it should be mandatory for all major trials to be overseen by people who are verifiably free from conflicts of interest. Not only should all major trials have to be registered a priori in order to be published, as major journals have finally decided,40 but complete trial protocols should be published or posted prior to unblinding, and final datasets should be made publicly available at the time of publication. Editors, reviewers, clinicians and patients should become much better at ‘detecting misleading claims in clinical research reports.’41 Everyone should be aware that initial reports of benefits are often reduced or contradicted when more and better research is carried out.42
While I can’t prove it here, I suspect that the vast majority of bias in the conduct, analysis and interpretation of medical research comes not from study participants but from researchers, analysts and interpreters. Before and after data are gathered there are many opportunities for investigators’ subjectivities and biases to come into play. The choice of what interventions to study, which outcomes to measure, which people to enrol and monitor, and how to conduct analyses and frame and interpret the results are highly subjective and value-laden. Null hypotheses, statistical assumptions such as one- or two-tailed testing, specific analytic methods, parameter cut-offs, algorithms, single vs. combined endpoints and methods of reporting (or not reporting) secondary measures are real human choices, and as such are subject to a potentially biasing influence on a number of levels. While it may be possible to require safeguards such as trial registration, advance-posting of trial methodology and blinding of investigators from treatment allocation, many potentially important investigator-associated biases will remain. Hopefully, these biases will be adequately minimised by a multi-tiered system of rigorous peer review, public accountability and professional ethics. The point here is that participant subjectivities and potential self-report biases are not the only sources of bias.
Placebo effects, meaning effects and mind–body interactions should be considered first as real and potentially important health modifiers, and second as potential sources of bias. Such influences should be considered carefully when designing and interpreting clinical research, not only as sources of bias, but also as potentially important health-modifiers. When the existence of a given specific effect is in question, rigorous double-blinded trials are in order. However, once a cause-and-effect relationship has been established beyond reasonable doubt, we should move from hypothesis testing to parameter estimation. Often, this could be done well with a large trial with four arms: (i) no treatment, (ii) blinded placebo (sham procedure), (iii) blinded treatment (real procedure) and (iv) unblinded treatment (procedure). Such trials would require twice as many participants as conventional dbRCTs but would produce more than twice the amount of useful data. With preparations and infrastructure in place, costs would be higher, but not double.
Before closing, I would like to introduce the concept of ‘sufficiently important difference’ (SID) as a benchmark for clinical significance and effect size. SID has been defined as the smallest amount of patient-valued benefit that an intervention would require in order to justify associated costs, risks and other harms,43 and has been assessed using benefit–harm trade-off methods.44 The four-armed trial outlined above would provide estimates of expected benefit using general and specific effect size. Whether or not these expected benefits would justify the treatment depends to a great degree on the costs and risks involved. For example, a safe and inexpensive treatment would require smaller expected benefits than a costly treatment with frequent side-effects or serious risks. Thus, clinical significance can only be judged within a specific treatment context, and should be judged from the patient’s perspective. This is important for the current discussion because it influences choice of hypothesised effect size when designing trials, as well as interpretation of results. It may also influence the incorporation of placebo/meaning/mind–body effects into clinical medicine. If acupuncture, meditation or a safe herbal medicine yields benefits equivalent to a costly medication with potentially significant adverse effects, the CAM method is preferred, regardless of mechanism of action. When positive placebo/meaning effects can be elicited safely and honestly, they should be, even when evidence is marginal.
In summary, we should (i) acknowledge and incorporate placebo and meaning effects into research and clinical practice, (ii) employ ‘no treatment’ and ‘unblinded’ groups in confirmatory clinical trials and (iii) set the benchmark for effect size as high as costs and risks dictate. Patient values should guide research, interpretation and translation into clinical practice. In the case where specific effects have already been well-proven, blinding may not always be necessary. What does it matter whether real health benefits arise from biological or psychological mechanisms? Once efficacy is proven, what matters most is how large and predictable the benefits are, and what costs and risks can be expected. If more than one effective treatment exists, then head-to-head trials may be warranted. For these, a two-by-two factorial design may be most appropriate, with no treatment, either treatment or both treatments as the four randomisation possibilities. Other RCT designs might also apply.45 In all cases, the people designing trials, interacting with participants and collecting, analysing and interpreting data must be appropriately open-minded, with no conflicts of interest or axes to grind. The participants in the trials need not always be blinded, but they should be honest and unprejudiced, and, importantly, representative of the population to which the results will be generalised. The sample size should be large enough so that the results are unambiguous. Carrying out such large, well-designed ‘pragmatic’46 trials will require substantial resources, as well as a rethinking of the goals and conceptual terrain of health-related research. If we recognise the potential importance of placebo effects, place patient-oriented outcomes at the top of our agenda and communicate well with those that allocate resources, we can make clinical research much more useful for clinicians and their patients.
