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Logo of nihpaAbout Author manuscriptsSubmit a manuscriptNIH Public Access; Author Manuscript; Accepted for publication in peer reviewed journal;
 
J Clin Epidemiol. Author manuscript; available in PMC Nov 1, 2012.
Published in final edited form as:
PMCID: PMC3146959
NIHMSID: NIHMS272257
Placebo effect studies are susceptible to response bias and to other types of biases
Asbjørn Hróbjartsson,1 Ted J Kaptchuk,2 and Franklin G Miller3
1 The Nordic Cochrane Centre, Rigshospitalet. Copenhagen, Denmark
2 Beth Israel Deaconess Medical Center, Harvard Medical School. Boston, MA. USA
3 Department of Bioethics, National Institutes of Health. Bethesda, MD. USA
Asbjørn Hróbjartsson: ah/at/cochrane.dk
OBJECTIVE
Investigations of the effect of placebo are often challenging to conduct and interpret. The history of placebo shows that assessment of its clinical significance has a real potential to be biased. We analyse and discuss typical types of bias in studies on placebo.
STUDY DESIGN AND SETTING
a methodological analysis and discussion.
RESULTS
The inherent nonblinded comparison between placebo and no-treatment is the best research design we have in estimating effects of placebo, both in a clinical and in an experimental setting, but the difference between placebo and no-treatment remains an approximate and fairly crude reflection of the true effect of placebo interventions. A main problem is response bias in trials with outcomes that are based on patients reports. Other biases involve differential co-intervention and patient drop-outs, publication bias, and outcome reporting bias. Furthermore, extrapolation of results to a clinical settings are challenging because of lack of clear identification of the causal factors in many clinical trials, and the non-clinical setting and short duration of most laboratory experiments.
CONCLUSIONS
Creative experimental efforts are needed to assess rigorously the clinical significance of placebo interventions and investigate the component elements that may contribute to therapeutic benefit.
Keywords: Placebo, placebo effect, response bias, bias, randomised trial, experiment
Scientific interest in the placebo effect has grown dramatically in the past two decades. Nevertheless, assessing the clinical relevance of this fascinating phenomenon is hampered by the difficulty in developing unbiased assessment of the effects of placebo interventions. In this article, we review the pervasive and complex connection between the placebo effect and bias.
After World War II, placebos were widely adopted as concurrent controls in randomized clinical trials to facilitate recruitment and retention and to control for bias (1). Interest in the “placebo effect” emerged out of the observation that patients in the placebo arm of these clinical trials often demonstrated significant improvement (2).
Henry Beecher popularized the concept of the placebo effect and brought it to the attention of the medical community in his classic 1955 JAMA article, “The Powerful Placebo” (3). Presenting a review of assorted placebo-controlled trials, he argued that the substantial improvement in the condition of patients receiving placebo was caused by the placebo intervention. His position implied two strong, but methodologically weak, claims: first, that placebo interventions caused large clinical effects on many patients across many clinical conditions, improving both patient-reported and observer-reported outcomes; second, that this assessment was reliable because it was based on randomized trials. Beecher saw placebo effects as a major source of bias in the assessment of treatment efficacy and his chief purpose in publicizing such a potential threat was to advocate for placebo-controlled trials (2). The concept of ‘powerful placebo’ became an established dogma in biomedicine.
Nevertheless, Beecher’s analysis committed the very fallacy that underlies the need for controlled trials. The observed response to placebo in randomized trials does not itself provide any reliable, unbiased, evidence of a placebo effect—an outcome caused by receiving a sham treatment disguised to be indistinguishable from an active (verum) medical intervention. Unbiased assessment of the placebo effect requires comparison of placebo interventions with a suitable control group in order to distinguish an effect of the placebo intervention from confounding factors, for example the natural history of the condition under investigation or regression to the mean (4). The flaws in Beecher’s approach were clearly recognized in the late 1990’s (5), but by that time the notion of ‘powerful placebo’ became deeply rooted.
Enhancing the scientific credibility of the placebo effect was the finding in 1978 that placebo analgesia could be blocked by the opioid antagonist naloxone (6), indicating that placebo analgesia can involve endogenous opiates (7,8). A further development in thinking about placebo was the application of brain imaging techniques from 2001 onwards sparking growing experimental investigation into neurobiological mechanisms of placebo effects, especially in pain (9).
Also in 2001, in sharp contrast, the power of the placebo was challenged by a systematic review published in The New England Journal of Medicine. The review identified 114 randomized clinical trials including placebo and no treatment groups, and reported no evidence of overall effects of placebo for objective and binary outcomes and a small, and doubtfully clinically relevant, effect for continuous subjective outcomes, such as pain (10). The findings were clearly incompatible with Beecher’s classic position. Some media commentators interpreted the result as demonstrating the placebo effect to be a myth (11), while other academic commentators either pointed out that worthwhile effects could still exist in some settings (12), or saw the review as a necessary scientific correction to set the bar differently for claims concerning placebo (13).
The review was updated in 2004 with similar findings (14), but the latest update from 2010 reported more multifaceted results (15). Large analgesic effects of placebo interventions were found in several well conducted trials. Furthermore, a considerable variation in effect could in part be explained by differences in trial design, for example, effect of placebo was larger when the intervention was a device (as compared with pill placebo).
The history of placebo shows that the assessment of the clinical significance of placebo has a very real potential to be biased. On the one hand, Beecher’s approach of analysing placebo groups without comparing with an untreated control group generates inflated estimations of placebo effects. Additionally, popular fascination with the placebo effect fuels unrealistic assessments of its therapeutic potential. The above-mentioned meta-analyses (1315), involving progressively larger numbers of studies and subjects, challenges the belief that in general the placebo is powerful. Yet it is unwarranted to conclude that placebo interventions are incapable of producing clinically meaningful benefit. It is generally not possible to prove a negative; moreover the meta-analyses (1315) identified several well-designed clinical trials with relatively large analgesic effects of placebo, and a general tendency for effects on patient-reported continuous outcomes. This, in addition to collateral evidence from laboratory experiments, points to the conclusion that placebo analgesia is a real phenomenon with the potential for clinical significance in some settings. However, estimating the size of the effect of placebo is subject to considerable uncertainty. The challenge in rigorously assessing the clinical benefit of placebo interventions is to reliably distinguish the magnitude of any real effect of placebo from the noise embedded in the human interaction of an experiment or a clinical trial. In this paper we explicate the types of bias that complicate the detection and measurement of clinically meaningful placebo effects.
In clinical epidemiology, bias constitutes deviation from the truth. As opposed to error caused by chance, bias represents a systematic distortion (16,17). The number of possible biases is large, and we make no claim for completeness.
The term ‘placebo effect’ is often used in a narrow meaning, implying the effect caused by a placebo intervention (or the treatment ritual). However, it is also used in a broader meaning implying the effect caused by a manipulation of the patient-doctor relationship, not necessarily involving a placebo intervention. In this paper we focus on trials and experiments comparing placebo with no-treatment, though the biases are equally relevant for trials and experiments comparing manipulations of the patient-provider interaction.
Biases in placebo research, such as response bias, can affect the internal validity of studies, raising doubts about whether, or to what extent, genuine placebo responses have been observed. Biases, such as publication bias, can also affect external validity, making the findings from experimental studies not accurately generalizable. In general, different types of biases may lead to overestimating or underestimating of the effects of placebo interventions. There is no clear evidence to support a ranking of which type of bias is more important, however, we consider response bias to play a major role (Table). Discussions of bias in controlled trials often focus on randomization and the need for concealment of allocation as a means to minimize selection bias. Selection bias is a general problem in clinical and experimental research (Table), and there is a large literature on the subject (18). In this paper, we have prioritized types of biases that we belief are more specific to the field of placebo.
Table
Table
Main types of challenges to the reliability and generalizability of randomised trials and experiments assessing the effect of placebo
The assessment of the placebo effect faces a basic conundrum. Patients may desire to please the researcher, or just give a “correct” or expected answer that fits with the experimental situation (1922). When patients report that they feel better after receiving a placebo intervention how do we know to which degree this reflects genuine symptomatic improvement, such as pain relief, that can be attributed to the placebo effect or a response bias? Patient-subjects who receive placebo interventions in clinical trials or laboratory experiments, believing that it was or may have been a real treatment, might be disposed to report positive outcomes to please the investigators with whom they had a clinical relationship. Conversely, those who did not receive any study intervention might be disappointed and disposed to report negative or “correct” outcomes.
This conundrum is posed by two different considerations. First, there is no blinded control for the placebo effect. Second, the placebo effect is most likely to play a role in the treatment of conditions in which the outcome targets are subjective (15), and necessarily based on introspective subject self-reports, for example pain. In controlled trials to assess the placebo effect (whether in clinical or laboratory settings), the placebo intervention is usually compared with a no-treatment control. Research subjects in the no-treatment arm necessarily know that they are not receiving treatment.
In assessing treatment efficacy of a pharmacological intervention with respect to subjective outcomes, such as relief of pain, blinded placebo-controlled trials are able to discriminate real effects from response bias. Patient-subjects may be disposed to report favorable outcomes by virtue of trial participation. But since they are randomized to masked drug or placebo, significant improvement in the treatment group as compared with the placebo group can be attributed to the efficacy of the treatment, as long as the masking conditions were successful. Response bias may operate to inflate the apparent drug effect (the difference between pre-trial baseline and the time of study outcome measurement); likewise, it may account for all or part of the response in the placebo arm. However, in view of randomization and blinding conditions, there is no reason to infer that the effect of response bias is greater in one arm than the other. In contrast, controlled trials to assess the placebo effect are not able to factor out response bias in this way, because they cannot be blinded.
Another important aspect of response bias is that it is likely to be closely associated with the same causal factors hypothesized to cause placebo effects: a warm patient-provider interaction and the doctor’s verbal and non-verbal suggestion of an important beneficial treatment effect. Thus, the more a physician signals friendliness and confident expectation of improvement, the less likely is the patient to disappoint the doctor who is making such an effort. Recent qualitative studies of patients in randomized clinical trials have demonstrated that patients can become dramatically attached to the research team and very committed the ‘success’ of a trial (23).
The conundrum of response bias is not limited to the typical clinical trial design. To elucidate the placebo effect, Benedetti and colleagues have deployed an experimental paradigm that compares the responses of patients to analgesic drugs in conditions of open and hidden administration (24). For post-surgical patients receiving open injections of drugs in the manner of a typical clinical encounter, a given dose of an opioid drug appears to produce a substantially greater reduction in pain as compared with patients who receive the same dose of drug via a computerized infusion pump but are not informed about when the drug will be administered (25,26).
This paradigm has been interpreted as demonstrating a clinically meaningful placebo effect, or the placebo component of active treatment, without the use of a placebo control. The results are impressive, but can we reliably distinguish between a real, greater reduction in pain in the open treatment group from a response bias, given that the patients knew that they were being given an analgesic drug and that they were participating in an experiment to assess analgesia? Likewise, those receiving the hidden infusion may have been negatively biased in their assessment of pain relief, knowing that they were suffering from pain but not knowing when pain medication would be administered. The open/hidden design is not itself able to rule out the alternative possibility of response bias.
A possible solution to the conundrum of response bias is to design trials assessing placebo effects with objective outcomes, not susceptible to patient behavior, and to blind the outcome assessor. This may be possible in some situations, such as studies of wound healing. However, even wound healing may be susceptible to variations in patient behavior; there is scant reliable evidence that placebo interventions modify objective outcomes in clinical trials (15); and what is important to patients is usually reduction in symptoms. Thus, trials with (only) objective outcomes would reflect a fairly limited number of clinically relevant problems.
Some have argued that neuroimaging technologies such as functional magnetic resonance (fMRI) and positron emission tomography (PET) can help determine whether placebo effects are independent of response bias (27). For example, one team of researchers has reported that placebo responses occur in pain-related areas of the brain during the time of stimulation and not only during assessment (28), while other researchers have shown that spinal cord mechanisms are involved with placebo analgesia (29). These experiments seem to indicate that at least some of the observed effect of placebo in an experimental setting is independent of response bias; however, they cannot rule out the hypothesis that some of the observed clinical effect is due to response bias.
In fact, other neuroimaging experiments point to potential involvement of response bias. For example, one study compared no-treatment to placebo treatment and placebo treatment plus naloxone. The placebo group reported significant pain reduction and the pain ratings of placebo treatment plus naloxone partially blocked the placebo behavioral response (30). But when one examines the simultaneous brain activation patterns of placebo with and without naloxone, there are inconsistencies. In the placebo treatment group, the average blood-oxygen-level-dependent (BOLD) response across all pain responsive brain regions decreased compared to controls. In the placebo treatment plus naloxone group, the BOLD actually shows that the naloxone group had increased activation compared to controls. For this group, instead of the partial blocking of pain sensitivity found in the behavioral data, there was brain activation that usually represents a worsening of pain (not a partial blocking of pain reduction). This finding suggests that what is reported is not necessarily congruent with what is felt, and, at least some of the time, pain self-reports due to placebo treatment are unrelated to the organic process of nociception.
While fMRI can measure hemodynamic blood oxygenation level dependent (BOLD) effect and PET can monitor regional cerebral blood flow and volume and map specific neuroreceptors using radiopharmaceuticals, neither method has advanced far enough to clearly and unequivocally distinguish to which extent the activations observed are “really” being felt by patients. In sum, just as there is no way to construct a blinded controlled trial to assess the placebo effect, so there is no way to eliminate subjectivity from patient-reported outcomes. This simply reflects the familiar but philosophically deep fact that there is no objective access to subjective experiences.
Patients receiving placebo, and believing they are receiving (or have a fair chance of receiving) genuine treatment are less likely to seek alternative treatment, or to modify their basic care treatment, so-called co-intervention bias. For example, in several large acupuncture trials for various pain conditions, the patients in the placebo group in general tended to take less analgesic medication as compared with the no-treatment group at post-treatment, despite similar levels of treatments at baseline (31). If the basic care of the patients was sub-optimal, and an increase in, for example, analgesic dose would influence pain, a difference in analgesic drug use would tend to underestimate the true effect of placebo.
Another type of bias relevant for trials assessing the effect of placebo is attrition bias -that is, the bias caused by patients dropping out of the trial. Patients in the no-treatment group may tend to drop out of the trial, or to skip examinations, or not follow the trial protocol, more frequently than the patients receiving placebo. In one well performed three-armed acupuncture pain trial running for 12 weeks, the drop-out rate in the acupuncture and placebo acupuncture group were comparable, 9% vs 6% (32). In the no-treatment group it was 16%. This illustrates the difference in patient behavior when included in placebo groups and no-treatment groups. The degree of bias involved, and its direction, is difficult to predict, and depend on whether those leaving the no-treatment group had better or worse outcomes than those who stayed.
Both co-intervention bias and attrition bias seem more likely to have an effect in trials of long duration. Thus, their potential impact would be smaller in studies of short duration. However, such studies face the problem that what is usually clinically most relevant is the longer-term result of a treatment.
Bias also can occur during analysis and reporting. It has become painfully clear that studies with positive results are more likely to be published than studies with a negative or neutral result, so-called publication bias (3335). Similarly, it has become clear that positive results within studies are more likely to be reported, and more likely to be reported in sufficient detail to be usable for meta-analyses, than negative results, so-called outcome reporting bias (36). Though most of the studies analyzing selective publishing of studies, and selective reporting of results, have focused on randomized trials, it seems likely that the same phenomenon applies to experimental research.
In experimental studies of placebo effects with no third active arm, the ‘interesting’ result is a positive outcome for those receiving placebo. It seems likely that the same motivations driving authors, reviewers, and editors to enhance publication of studies with large effects of experimental interventions in general, also apply to the field of placebo research. This would mean that studies reporting large effects of placebo are published in prestigious journals, whereas studies with no effects would be dismissed as ‘failed experiments’, and are published less often, later, in less prestigious journals and more often as abstracts.
Matters are somewhat more complicated in three-armed trials aimed at assessing specific treatment efficacy, as the primary drive for publication bias and outcome reporting bias relate to the effect of the active treatment, and it is difficult to predict how this affects the publishing and reporting of results of placebo. However, the pooling of results from placebo and no-treatment groups is a problem. Several examples of such pooling based on a lack of statistical difference between placebo and no treatment has been published (22,36), though it is difficult to assess how often it takes place. In one trial of immunotherapy for ragweed allergy the placebo and no-treatment group were combined because of ‘no statistically difference’ in symptom score (33). Hopefully, the ongoing efforts to establish trial registers, and to have public access to trial protocols, will diminish this problem in the long run, also for placebo research (37).
It is always challenging to extrapolate study results from the controlled framework of a clinical trial or a laboratory-based experiment to the normal clinical encounter. However, within placebo research this mental and methodological leap is more difficult than usual. One reason for this in clinical trials assessing placebo effects is what could be called ‘causal indeterminateness”. A normal placebo-controlled trial is designed to isolate the hypothesized causal factor that is the only difference between the treatment and the placebo control. For example, in a trial of the effect of a drug on irritable bowel syndrome the hypothesized causal factor (the drug) is an inherent component of the intervention (the tablet). However, if the trial also involved a comparison between the placebo intervention and a no-treatment/usual care group, the causal factors that may be responsible for improved symptoms in the placebo group are not isolated, as they are for the drug group. Instead, they form a set of putative causal factors, including the physical appearance of the pill, the ritual of pill taking, and positive expectations associated with taking an intervention, which may be believed to be an active treatment (because it is indistinguishable from the drug intervention). In other words, the placebo intervention serves as a kind of causal surrogate for the true underlying causal factors.
One example of ‘causal indeterminateness’ concerns the possible interpretations of the effects of placebo acupuncture. Large three-arm trials including traditional acupuncture, sham intervention, and no-treatment/usual care groups report considerable effect of real and sham acupuncture on pain, but no difference between them (31). Acupuncture as well as sham acupuncture are complex interventions, which include a host of factors that may be causally responsible for placebo effects. One interpretation is that the true causal factors are the repetitive and prolonged treatment sessions involving a high degree of interaction between convinced acupuncturists and patients with a positive view of alternative medicine. In addition, the perception of needling—an invasive intervention, which may seem novel and exotic for acupuncture naïve patients—may contribute to positive expectations. Another interpretation is that the effects reflect, in part, lack of disclosure to patients that they could receive placebo, which is common (and ethically problematic) in these studies (38). This interpretation is in accord with the notion that the process of randomisation and informed consent may, at least for some outcomes, influence the effects of placebo (39). A third interpretation is that sham needling has a physiological analgesic effect, unrelated to the patient-provider interaction. Thus, we have no clear grasp of what are the true causal factors at play, and the various interpretations would have quite different clinical implications.
In laboratory studies it is possible to control the experimental situation more than in the standard clinical trial, but the main problem with laboratory studies is that they are far removed from the normal clinical situation. Non-clinical experimental studies on placebo almost always evaluate outcomes of very short duration, lasting for hours or a few days, and often involve healthy volunteers. Furthermore, the highly controlled environment with interactions of relatively long duration with laboratory personnel differs substantially from the hectic and uncontrolled environment of the normal clinical encounter, which usually is of comparatively short duration. The mechanistic laboratory studies are aimed at exploring the biological basis for placebo effects, and not at evaluating the effect of placebo in the normal clinical situation.
Thus, it is difficult to reliably extrapolate the results of placebo studies without 1) a better understanding of the causal factors and 2) a study framework that is designed to isolate the causal factors of interest and is as close to the clinical situation as possible. One strategy to address this problem of causal indeterminateness is to design clinical trials in which the presumed causal factors are characterized a priori, and implemented in accordance with a discrete protocol. For example, a trial may be designed to test the effect of a ‘placebo intervention package’ consisting of a well-defined treatment provider approach to a patient, for example a specific placebo intervention in combination with a positive consultation. Further studies might vary the components of the placebo intervention package to determine the relative contributions of discrete elements to the size of placebo effects. Although hampered by logistical and financial challenges, this may be a promising avenue for further research (40, 41). Progress in translating placebo research into clinical practice depends on developing hypotheses relating to the causal factors responsible for placebo effects in the clinical setting and designing rigorous experiments to test them.
Despite methodological limitations, randomization to placebo and no-treatment is the best research design we have in estimating effects of placebo, both in a clinical and in an experimental setting. However the design remains an approximate and fairly crude method for assessing the true effect of placebo interventions. The conundrum of response bias when outcomes are patient-reported, and other biases make study results challenging to interpret. The placebo effect and its various mechanisms of action is of great interest for neuroscience; however, its interest for medicine depends primarily on the extent to which placebo interventions can be found to produce reliable and clinically relevant therapeutic benefits. Creative experimental efforts are needed to assess rigorously the clinical significance of placebo interventions and investigate the component elements that may contribute to therapeutic benefit.
Acknowledgments
NCCAM-NIH grant # K24 AT004095 funded TJK for work on this analysis. Kong Jian provided valuable feedback.
Footnotes
The opinions expressed are the views of the author and do not necessarily reflect the policy of the National Institutes of Health, the Public Health Service, or the U.S. Department of Health and Human Services.
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