The placebo response.

Abstract

The placebo response applies not only to phase II, but also to phase III studies and has clearly played a significant role in changing the way researchers need to approach conducting trials. Let us first begin by defining the term randomized controlled trial assay sensitivity. This is the ability of a clinical trial to distinguish an effective treatment from a less effective or ineffective intervention. Without assay sensitivity, a trial is not capable of comparing the efficacy of the two interventions and is therefore not internally valid (HHS, 2001). This is really the principle that underlies why we do randomized controlled trials, because we are interested in a valid discrimination between the specific effect of a treatment and other effects that patients might undergo as part of the therapy. However, when researchers think about assay sensitivity we normally think about laboratory tests, but in fact, any testing paradigm really can be considered in terms of its ability to detect a real difference if a real difference exists (Dworkin et al., 2012). Conducting a clinical trial involves multiple steps, each of which needs to be considered to increase the study's ability to distinguish treatment effects. Principally, researchers should be cognizant of the appropriateness of the clinical question, selecting the suitable patient population, trial design, time frame, measures to be assessed, analysis and interpretation of the data, and the publication of their findings. In terms of thinking about study design characteristics, researchers should consider the population/patient characteristics, enrollment criteria and procedures, study site characteristics, outcomes and measurement issues, limiting the occurrence of missing data, and the differentiation of a placebo response vs. an active treatment response (Dworkin et al., 2012). Differentiating the response in the placebo group vs. the active treatment group is critical. By definition, a placebo is “a harmless pill, medicine, or procedure prescribed more for the psychological benefit to a patient than for the physiological effect.” Understanding this definition depends on which dictionary is used. Some dictionaries reference mental processes instead of psychological benefit. This is an important point. What we have learned from neurology and neuroscience over the last 20 or 30 years is that the psychological benefit really is all in the individual's head. The processing of nociceptive input and the perception of pain occurs in the brain. There are very clear, neurologically definable, substrate definable, and pathway definable processes that affect all of the aspects of response to our environment. Another way of thinking about placebos is as the non-specific effect of a treatment as compared with the specific effect. In pain therapy most of the patients who are seen feel better when they leave. Why? Because the patient made an investment in time and effort to come in and be seen by their physician. They feel that somebody is paying attention to them and is trying to help them. The whole process makes a difference in the way their brain functions. The placebo effect is the mind–body effect brought about by the belief in a therapy. It is not an inactive therapy. It is a physiologic process mediated by neurotransmitters, neuro-firing, signaling, transmission, and all the other components that change in the state of the target tissues. There is something that goes on within the central nervous system that affects the descending systems and then affects some distal neural tissue. In pain management, it is about preventing the input of nociception that has influence over a host of other phenomena in the body and changes in the central nervous system response that mediate the perception of sensory input. In depression, the issue of the placebo effect in clinical trials is seen extensively. Depression is a brain-mediated phenomenon. It involves a host of processes. Antidepressants exert a drug-related change in the state of the brain and a non-specific effect which is the drug independent change in the state of the brain. In contrast, what is the specific effect of psychotherapy? How do you quantify the effect in comparison to antidepressants? Well-designed clinical trials provide the opportunity to quantify these effects. The strength of the clinical trial is in the process of randomization and the equilibration of the two groups that are being compared. The intention of the placebo arm is to provide a comparator and to control for the known variables, such as the natural history of disease, the regression to the mean phenomenon that happens in every trial, and the placebo effect. The intention of the therapy group is also to assess the natural history of the disease, regression to the mean, and placebo effect, in addition to the specific effect of the therapy. A review of the data from depression trials suggests that the response to placebo in published studies of antidepressant medication for patients with major depressive disorder is highly variable, often substantial, and has increased significantly in recent years. Data from a review of 75 studies identified that the mean proportion of patients in the placebo group who responded to therapy was 29.7% (8.3%) (range, 12.5%–51.8%). Most studies reviewed examined more than a single active medication. In the active medication group with the greatest response, the mean proportion of patients responding was 50.1% (9.0%) (range, 31.6%–70.4%) (Walsh et al., 2002). A closer look at pain studies reveals that the placebo response rates vary from 15% to 50%, and are partially dependent on the type of pain. There is no clear evidence of change over time but the placebo effect is very often blamed for the failure of trials to show a statistical significance (Finnerup et al., 2005). It has been shown that a larger placebo response is associated with a lower likelihood of a statistically positive study. This does not prove that the higher group placebo rate causes the study failure. It also does not prove that excluding placebo responders would change the results (Katz et al., 2008). Reducing the placebo group response rate statistically would mean that the comparison of change in group levels is harder to detect the closer the underlying group response is to 0.5% or 50%. The measurement or ceiling effects would also be altered. Getting closer to the top of a scale results in trouble demonstrating a difference and reduction in the size of the detectable difference between groups. Also, if you increase the size of the study group, you will have a better chance of showing a difference. Strategies to minimize the placebo response include standardizing recruitment to be inclusive of patients with varying severity and longevity of disease symptoms; staff training, controlling patient's expectations; longer studies, and excluding patients likely to be placebo responders (Fava et al., 2003). Is using a placebo run-in period prior to randomization to active treatments a viable option? A meta-analysis of 101 studies of acute phase antidepressant drug efficacy in patients with major depression revealed that a placebo run-in does not lower the placebo response rate, increase the drug-placebo difference, or affect the drug response rate post-randomization (Trivedi and Rush, 1994). Why is that? It is because when you are taking out people in the placebo treated group you are not taking out only people who have a mind–body placebo response who are likely to be in the trial, you are taking out patients who have a natural history of disease and regression to the mean. In the next phase, there is a reasonable likelihood that because of natural history or regression to the mean, they are going to get better. We hypothesized that subjects with higher baseline variability will have a higher response in the placebo treated group and that excluding subjects with higher baseline variability would increase the assay sensitivity of pain RCTs. To evaluate the role of baseline pain variability in placebo group response and the differentiation of treatment effect, we undertook a study utilizing available clinical trial data from new drug applications from the Food and Drug Administration (FDA). Twelve studies were identified. The data was harmonized. We then looked at the study design features and tried to look at the number of sites, number of adverse events, etc. However, even with 12 trials there was not enough variability in those data to be able to use them effectively in the model. The response rate was defined as a change of 30% in their 0–10 scale. In examining the demographics we noted that in the studies themselves there was no difference between the placebo and treated group in the demographics. However, there was quite a difference between the peripheral neuropathy (PHN) study groups and the diabetic peripheral neuropathy (DPN) groups. Specifically, differences were seen in the patient's age, the distribution of men and women, weight, and the body mass index. This necessitated a mixed model approach to look at the two diseases separately, because two patient groups are likely to respond differently or could potentially respond differently to this kind of process. The model for PHN demonstrated that the baseline standard deviation (the 0–10 scale at the baseline taken over 7 days) had a significant interaction with treatment that was associated with the patients in the placebo group differently than in the treatment group. We also found that age had an effect in this particular model. Older patients had a lower chance of response to the placebo and a similar response in treatment group. Gender and weight affected the responses, both in the treatment and placebo group in the same way. In the DPN model, we found that the results were consistent with a 50% change in pain and reports of “Much Better” on the Patient Global Impression of Change (PGIC) scale. In reviewing their diaries, there was about a 1.2, slightly higher chance of responding in the placebo group if you had a higher level of variability in your baseline diary; and relatively less, although a little bit of an effect in the treatment group. To assess these data we developed a formula to simulate: “If we had excluded patients with that amount of standard deviation variability, how much of a difference would it have made in the efficiency of the trial?” This permitted us to look at just the standard deviation and at the probability of response in the treatment group vs. the probability of response in the placebo group for each individual patient. In the PHN groups we identified that with no exclusions, you needed about 90 patients per group in order to find a statistically significant difference. Using a ratio of 1 : 1, there is a little bit of difference between the groups. If you utilize a 1.5 value, there is a substantial benefit in terms of the efficiency of the trial. In this instance only 65 patients are needed to demonstrate a difference. In the DPN group, the numbers were similar. These data suggest that you could use fewer patients and have a higher chance of demonstrating a statistically significant difference (Zhang et al., 2011).