JL, SV, and DM designed the re-analysis, conducted data analysis, and wrote the current manuscript. DM, LP, LC, AT, and MF designed and conducted the original randomized controlled trial this re-analysis is based on. LB and AJC assisted with the statistical analysis. GP and AC assisted with the writing of the manuscript.

### FUNDING

The original study was supported by the NIH and the National Center for Complementary and Alternative Medicine (NCCAM), R01 grant R01AT001638. SAMe tosylate and matching placebo were supplied by Pharmavite LLC, CA, United States. JL was supported by a fellowship within the Postdoc-Program of the German Academic Exchange Service (DAAD).

both blinded and non-blinded outcome assessors. BMJ (2012) 1119:1–11. doi: 10.1136/bmj.e1119

**Disclaimer:** The article reflects the views of the authors and may not reflect the opinions or views of all the study investigators, the NIH, or the NCCAM.

**Conflict of Interest Statement:** JL was supported by a fellowship within the Postdoc-Program of the German Academic Exchange Service (DAAD).

LP has received research support from Neuronetics, NIH, HRSA, and NeoSync. He has served on advisory panels for Abbott and AstraZeneca. He has served as a consultant to Gerson Lehrman, Wiley, Springer, Qatar National Research Fund, and Abbott.

LC has received research support from Neuronetics, NIH, and NeoSync. She has served on advisory panels or provided consulting services for Abbott, Corcept, Johnson &Johnson, and Takeda-Lundbeck.

AT has received research support from Neuronetics, NeoSync, and NIH.

GP has served as a consultant for Abbott Laboratories, Acadia Pharmaceuticals, Inc∗ , Alkermes, Inc, AstraZeneca PLC, Avanir Pharmaceuticals, Axsome Therapeutics∗ , Boston Pharmaceuticals, Inc., Brainsway Ltd, Bristol-Myers Squibb Company, Cephalon Inc., Dey Pharma, L.P., Eli Lilly Co., Genentech, Inc∗ , Genomind, Inc∗ , GlaxoSmithKline, Evotec AG, H. Lundbeck A/S, Inflabloc Pharmaceuticals, Janssen Global Services LLC∗ , Jazz Pharmaceuticals, Johnson & Johnson Companies∗ , Methylation Sciences Inc, Mylan Inc∗ , Novartis Pharma AG, One Carbon Therapeutics, Inc∗ , Osmotica Pharmaceutical Corp.∗ , Otsuka Pharmaceuticals, PAMLAB LLC, Pfizer Inc., Pierre Fabre Laboratories, Ridge Diagnostics (formerly known as Precision Human Biolaboratories), Shire Pharmaceuticals, Sunovion Pharmaceuticals, Taisho Pharmaceutical Co, Ltd, Takeda Pharmaceutical Company LTD, Theracos, Inc., and Wyeth, Inc.

GP has received honoraria (for lectures or consultancy) from Abbott Laboratories, Acadia Pharmaceuticals Inc, Alkermes Inc, Asopharma America Cntral Y Caribe, Astra Zeneca PLC, Avanir Pharmaceuticals, Bristol-Myers Squibb Company, Brainsway Ltd, Cephalon Inc., Dey Pharma, L.P., Eli Lilly Co., Evotec AG, Forest Pharmaceuticals, GlaxoSmithKline, Inflabloc Pharmaceuticals, Grunbiotics Pty LTD, Jazz Pharmaceuticals, H. Lundbeck A/S, Medichem Pharmaceuticals, Inc, Meiji Seika Pharma Co. Ltd, Novartis Pharma AG, Otsuka Pharmaceuticals, PAMLAB LLC, Pfizer, Pharma Trade SAS, Pierre Fabre Laboratories, Ridge Diagnostics, Shire Pharmaceuticals, Sunovion Pharmaceuticals, Takeda Pharmaceutical Company LTD, Theracos, Inc., Titan Pharmaceuticals, and Wyeth Inc.

GP has received research support (paid to hospital) from AstraZeneca PLC, Bristol-Myers Squibb Company, Forest Pharmaceuticals, the National Institute of Mental Health, Neuralstem, Inc, PAMLAB LLC, Pfizer Inc., Ridge Diagnostics (formerly known as Precision Human Biolaboratories), Sunovion Pharmaceuticals, Tal Medical, and Theracos, Inc.

GP has served (not currently) on the speaker's bureau for BristolMyersSquibb Co and Pfizer, Inc.

∗Asterisk denotes activity undertaken on behalf of Massachusetts General Hospital.

MF: All disclosures can be view on line at: http://mghcme.org/faculty/facultydetail/maurizio\_fava

**Research Support**: Abbott Laboratories; Acadia Pharmaceuticals; Alkermes, Inc.; American Cyanamid;Aspect Medical Systems; AstraZeneca; Avanir Pharmaceuticals; AXSOME Therapeutics; Biohaven; BioResearch; BrainCells Inc.; Bristol-Myers Squibb; CeNeRx BioPharma; Cephalon; Cerecor; Clintara, LLC; Covance; Covidien; Eli Lilly and Company;EnVivo Pharmaceuticals, Inc.; Euthymics Bioscience, Inc.; Forest Pharmaceuticals, Inc.; FORUM Pharmaceuticals; Ganeden Biotech, Inc.; GlaxoSmithKline; Harvard Clinical Research Institute; Hoffman-LaRoche; Icon Clinical Research; i3 Innovus/Ingenix; Janssen R&D, LLC; Jed Foundation; Johnson & Johnson Pharmaceutical Research & Development; Lichtwer Pharma GmbH; Lorex Pharmaceuticals; Lundbeck Inc.; Marinus Pharmaceuticals; MedAvante; Methylation Sciences Inc; National Alliance for Research on Schizophrenia & Depression (NARSAD); National Center for Complementary and Alternative Medicine (NCCAM);National Coordinating Center for Integrated Medicine (NiiCM); National Institute of Drug Abuse (NIDA); National Institute of Mental Health (NIMH); Neuralstem, Inc.; NeuroRx; Novartis AG; Organon Pharmaceuticals; Otsuka Pharmaceutical Development, Inc.; PamLab, LLC.; Pfizer Inc.; Pharmacia-Upjohn; Pharmaceutical Research Associates., Inc.; Pharmavite&174; LLC; PharmoRx Therapeutics; Photothera; Reckitt Benckiser; Roche Pharmaceuticals; RCT Logic, LLC (formerly Clinical Trials Solutions, LLC); Sanofi-Aventis US LLC; Shire; Solvay Pharmaceuticals, Inc.; Stanley Medical Research Institute (SMRI); Synthelabo; Taisho Pharmaceuticals; Takeda Pharmaceuticals; Tal Medical; VistaGen; Wyeth-Ayerst Laboratories

**Advisory Board/Consultant**: Abbott Laboratories; Acadia; Affectis Pharmaceuticals AG; Alkermes, Inc.; Amarin Pharma Inc.; Aspect Medical Systems; AstraZeneca; Auspex Pharmaceuticals; Avanir Pharmaceuticals; AXSOME Therapeutics; Bayer AG; Best Practice Project Management, Inc.; Biogen; BioMarin Pharmaceuticals, Inc.; Biovail Corporation; BrainCells Inc; Bristol-Myers Squibb; CeNeRx BioPharma; Cephalon, Inc.; Cerecor; CNS Response, Inc.; Compellis Pharmaceuticals; Cypress Pharmaceutical, Inc.; DiagnoSearch Life Sciences (P) Ltd.; Dinippon Sumitomo Pharma Co. Inc.; Dov Pharmaceuticals, Inc.; Edgemont Pharmaceuticals, Inc.; Eisai Inc.; Eli Lilly and Company; EnVivo Pharmaceuticals, Inc.; ePharmaSolutions; EPIX Pharmaceuticals, Inc.; Euthymics Bioscience, Inc.; Fabre-Kramer Pharmaceuticals, Inc.; Forest Pharmaceuticals, Inc.; Forum Pharmaceuticals; GenOmind, LLC; GlaxoSmithKline; Grunenthal GmbH; Indivior; i3 Innovus/Ingenis; Intracellular; Janssen Pharmaceutica; Jazz Pharmaceuticals, Inc.; Johnson & Johnson Pharmaceutical Research & Development, LLC; Knoll Pharmaceuticals Corp.; Labopharm Inc.; Lorex Pharmaceuticals; Lundbeck Inc.; Marinus Pharmaceuticals; MedAvante, Inc.; Merck & Co., Inc.; MSI Methylation Sciences, Inc.; Naurex, Inc.; Navitor Pharmaceuticals, Inc.; Nestle Health Sciences; Neuralstem, Inc.; Neuronetics, Inc.; NextWave Pharmaceuticals; Novartis AG; Nutrition 21; Orexigen Therapeutics, Inc.; Organon Pharmaceuticals; Osmotica; Otsuka Pharmaceuticals; Pamlab, LLC.; Pfizer Inc.; PharmaStar; Pharmavite R LLC.; PharmoRx Therapeutics; Precision Human Biolaboratory; Prexa Pharmaceuticals, Inc.; PPD; Purdue Pharma; Puretech Ventures; PsychoGenics; Psylin Neurosciences, Inc.; RCT Logic, LLC (formerly Clinical Trials Solutions, LLC); Relmada Therapeutics, Inc.; Rexahn Pharmaceuticals, Inc.; Ridge Diagnostics, Inc.; Roche; Sanofi-Aventis US LLC.;

**Stock/Other Financial Options**: Equity Holdings: Compellis; PsyBrain, Inc.

Royalty/patent, other income: Patents for Sequential Parallel Comparison Design (SPCD), licensed by MGH to Pharmaceutical Product Development, LLC (PPD) (US\_7840419, US\_7647235, US\_7983936, US\_8145504, US\_8145505); and patent application for a combination of Ketamine plus Scopolamine in Major Depressive Disorder (MDD), licensed by MGH to Biohaven. Patents for pharmacogenomics of Depression Treatment with Folate (US\_9546401, US\_9540691).

Copyright for the MGH Cognitive & Physical Functioning Questionnaire (CPFQ), Sexual Functioning Inventory (SFI), Antidepressant Treatment Response Questionnaire (ATRQ), Discontinuation-Emergent Signs & Symptoms (DESS), Symptoms of Depression Questionnaire (SDQ), and SAFER; Lippincott, Williams & Wilkins; Wolkers Kluwer; World Scientific Publishing Co.Pte.Ltd.

DM has received research support from the Bowman Family Foundation, Nordic Naturals, and PharmoRx. He has provided unpaid consulting for Pharmavite LLC and Gnosis USA, Inc. He has received writing honoraria from Pamlab and Nordic Naturals, and speaking honoraria from Blackmores, and the MGH Psychiatry Academy. He has received royalties from Lippincott Williams & Wilkins, for textbook "Natural Medications for Psychiatric Disorders: Considering the Alternatives" (DM and Jerrold F Rosenbaum, Eds.).

The remaining authors declare that the research was conducted in the absence of any commercial or financial relationships that could be construed as a potential conflict of interest.

Copyright © 2018 Laferton, Vijapura, Baer, Clain, Cooper, Papakostas, Price, Carpenter, Tyrka, Fava and Mischoulon. This is an open-access article distributed under the terms of the Creative Commons Attribution License (CC BY). The use, distribution or reproduction in other forums is permitted, provided the original author(s) and the copyright owner(s) are credited and that the original publication in this journal is cited, in accordance with accepted academic practice. No use, distribution or reproduction is permitted which does not comply with these terms.

# Mental Training for Better Achievement: Effects of Verbal Suggestions and Evaluation (of Effectiveness) on Cognitive Performance

#### Kristina Fuhr\* and Dustin Werle

Clinical Psychology and Psychotherapy, Department of Psychology, University of Tuebingen, Tuebingen, Germany

Objective: There is only some literature regarding the influence of verbal suggestions on cognitive performance in healthy volunteers. For example, the performance in a knowledge test was enhanced when participants were told that they had subliminally received the correct answer. However, enhancing cognitive performance only via verbal suggestions without prior conditioning phases has not yet been examined. The goal of our study was therefore to investigate the effects of a mental training based on verbal suggestions compared to a control training on cognitive performance in a student population using a balanced-placebo-design.

Edited by:

Katja Weimer, Universität Ulm, Germany

#### Reviewed by:

Cosima Locher, Universität Basel, Switzerland Karin Meissner, Ludwig-Maximilians-Universität München, Germany

\*Correspondence: Kristina Fuhr<EMAIL_ADDRESS>
#### Specialty section:

This article was submitted to Psychosomatic Medicine, a section of the journal Frontiers in Psychiatry

Received: 21 June 2018 Accepted: 27 September 2018 Published: 22 October 2018

#### Citation:

Fuhr K and Werle D (2018) Mental Training for Better Achievement: Effects of Verbal Suggestions and Evaluation (of Effectiveness) on Cognitive Performance. Front. Psychiatry 9:510. doi: 10.3389/fpsyt.2018.00510 Methods: In total, 103 participants were randomly assigned either to listening to a 20 min audio-taped mental training or to a 20 min philosophy lecture (control training) via headphones. Participants were individually tested before and after the training concerning their cognitive performance. Information about the type of training were varied in both intervention conditions ("You are part of our experimental condition and you will receive an effective mental training" or "You are part of our control group and you will receive the control condition"). At the end of the assessment, participants were asked what kind of training they believed they had received and how effective they would rate the received training.

Results: Overall, the cognitive performance improved in all participants, F (1, 99) = 490.01, p < 0.001. Contrary to our hypotheses, we found no interaction of the type of training and type of instruction on the cognitive performance. Participants who rated the received training as being effective at the end of the experiment (regardless if it was the mental or the control training), have before experienced a greater improvement in their cognitive performance [F (2,100) = 7.26, p = 0.001] and showed higher scores in the ability to absorb [F(2, 99) = 3.75, p = 0.027].

Conclusion: The subjects' own experiences in the task might have influenced the rating of the training rather than the actual training or the information they receive regarding the type of training. This finding underlines the relevance of enhancing the subjective beliefs and self-efficacy in situations where cognitive attention processes are important and of individually tailoring mental trainings.

Keywords: placebo, mental training, cognitive performance, verbal suggestions, effectiveness rating

## INTRODUCTION

The influence of expectations and suggestions on the placebo response was shown in different experimental studies concerning psychological aspects like for example pain [e.g., (1)]. In the context of pain, the given verbal instructions did not only influence the subjective analgesic effect but also reduced the amount of requests for opioid doses (1). However, verbal suggestions alone (without any preconditioning) could only influence pain tolerance in healthy subjects and motor performance in Parkinson's patients, but not for example hormonal secretion (2). Little is known about placebo effects on cognitive performance. For example, cognitive processes like attention could be improved after suggesting participants they had consumed caffeine similar to the improvement after they really consumed caffeine [e.g., (3)]. Comparable results were found when college students believed that they had received a "neuro-enhancing" stimulant. The cognitive performance improved in some scales and the participants also evaluated their subjective results as better (4). However, the placebo effect concerning the cognitive processes was only investigated when providing the participants with some kind of substance or placebo. Therefore, it would be interesting if similar to the results that were found in pain, cognitive processes might also be influenced by evoking specific expectations just via receiving verbal suggestions, i.e., verbal instructions but also via psychological interventions. Automatic visual perception and cognitive processes, as they are for example assumed for the Stroop effect, can be influenced and even controlled just by receiving verbal suggestions during a hypnotic experience. This effect was most pronounced in highly suggestible individuals (5, 6). For example, the interference in the Stroop effect, when the ink color and the word color are incongruent, could be eliminated when suggesting subjects to view word stimuli as neutral and meaningless (5). Furthermore, the performance of counting visual stimuli was reduced when suggesting participants after a hypnotic induction that a wooden board would cover the screen (6). In one study, the performance in the Flanker task, for example, was only influenced by posthypnotic suggestions in highly suggestible participants compared to (the same) nonhypnotic suggestions in an alert state (7). Thus, the advantage of using verbal suggestions after a hypnotic induction or with highly suggestible participants instead of only verbal instructions is that hypnotic suggestions were able to even demonstrate control over some cognitive processes, as described before (5, 6). However, there is only some literature regarding the enhancement of cognitive performance only via verbal suggestions. For example, the performance in a knowledge test was enhanced when participants believed that they had subliminally received the correct answer (placebo condition) compared to those who were told that they subliminally only received a flash [control condition, (8)]. Even the results in an intelligence test could be enhanced when positive expectations were evolved only via the way participants were recruited (9). Another study found that it was more the subjective evaluation of the own performance that was influenced by expectations rather than the objective performance [as for example reaction times or success rates, see (10)]. However, in previous studies, expectancy effects on placebo were usually paired with some previous test phase in which participants already underwent a specific conditioning paradigm and therefore could already build according expectations regarding the relevant test phase (10).

Taken together, previous results imply that some suggestions can block cognitive processes that were assumed to be automatic and not directly influenceable. However, the magnitude of the placebo effect on enhancing cognitive performance only based on verbal suggestions without previous experience has not yet been examined.

Concerning placebo effects in psychotherapy, as in wellestablished treatments like for example cognitive behavioral therapy, it is impossible to conduct double-blind trials and challenging to develop "placebo" control groups that are not distinguishable from the specific treatment that is to be tested (11). However, it was demonstrated that psychological placebo interventions show equivalent effects as specific psychotherapies if they were structurally equally designed (12). That's why some researchers emphasize the relevance/superiority of the "common factors" in psychotherapy over the specific therapeutic ingredients (13, 14). Investigating mechanisms of change and differentiating specific and non-specific/common therapeutic "ingredients" is more or less impossible since every specific ingredient is transmitted also via words, verbal suggestions, and other therapeutic rituals (15). Studies are lacking that directly manipulate some of the non-specified factors as for example expectations (16). Using hypnotic verbal suggestions could be one possibility to use some kind of psychological intervention that is not based on specific treatment strategies but directly addresses the non-specific factors like expectations (17) and hypnosis can thus be used as a "non-deceptive placebo" (18).

The goal of our study was therefore to investigate the effects of a mental training based on hypnotic verbal suggestions compared to a control training consisting of a philosophy lecture on the cognitive performance in a student population using a "balanced-placebo-design" (19). We paired the trainings with evoking different expectations in the participants concerning the "efficacy" of the mental training. We expected the strongest effects on cognitive performance when participants received both the mental training and the suggestion of this training as being "effective" compared to the conditions in which they received incongruent information (received mental training and were told "ineffective" or received control training and were told "effective") or the control training paired with the information of being "ineffective."

### MATERIALS AND METHODS

#### Study Design

The study used a mixed 2 × 2 × 2 design with the within-factor time and the between-factors intervention and information, see **Figure 1**. As dependent variable, we assessed the cognitive performance in a specific attention/concentration task (see Assessments). With the within-factor time, cognitive performance was measured before and after the intervention. The factor intervention consisted of the mental training vs.

the control training. Concerning the factor information, half of the participants of each intervention condition was told to receive an effective training ("You are part of our experimental group and you will receive an effective mental training") vs. the other half was told that they are part of the control group ("You are part of our control group and you will receive the control condition"). With pairing the factors intervention and information, a balanced-placebo-design was established. Subjects were randomly assigned to one of the four experimental conditions. We chose random numbers between one to four that were equally distributed to do so (source: https://rechneronline. de/zufallszahlen/).

The study protocol was approved by the local Ethics Committee for Psychological Research of the Faculty of Science at the University of Tuebingen (Az 2016/1123/26). All subjects gave written informed consent in accordance with the Declaration of Helsinki.

### Participants

The a priori sample size was defined at 100 participants.

Participants for the current study were recruited at the University of Tuebingen via announcements in social media (e.g., facebook groups of psychology students and of the students who were interested in study participation) and in cafeterias and libraries. Inclusion criteria were (1) being at the age of 18 to 50 years old, (2) no uncorrected ametropia, (3) normal hearing, and (4) providing written informed consent to participate in the study. Participants were alerted to the fact that they might be incompletely informed about some part of the study ["authorized deception," see (20)]. After study completion, every participant was completely debriefed in case of prior deception. The "misinformation" of participants was necessary in these experimental conditions where the type of intervention and the type of information were not congruent (mental training and told that "being part of the control group"; control training and told that "being part of the experimental group and receiving an effective training"). The goal of the incomplete information was to evoke specific expectations in participants concerning the effectiveness of the following intervention. The so-called "authorized deception" is a possibility in experimental placebo studies to overcome an important ethical dilemma. On one hand, the deception of participants is necessary to demonstrate the effect of expectancy on outcome. On the other hand, the ethical norms request the participant's free choice of taking part in a study only after every aspect of the study was fully displayed (21). It was shown that the use of "authorized deception" does not affect the placebo effect and therefore is a very useful tool (20).

In total, 103 participants were investigated in the present study. Eighty-three of the subjects (80.6%) were female, all of them being students, about 50% were studying psychology (n = 43, 41.7%) or cognitive science (n = 10, 9.7%) in the first or second year. The mean age was 23.35 years (SD = 4.18).

### Interventions

In both conditions, participants individually listened to a 20 min audio-take via headphones. The mental training consisted of different indirect hypnotic verbal suggestions for enhancing the cognitive performance: reminding participants of their own experience when learning some new procedures, creating the image of an archer, giving metaphors with the goal to concentrate and focus on relevant aspects of a task whereas irrelevant aspects can be ignored. Participants were thus not directly but indirectly told to focus more on the cognitive performance task. The control training consisted of a part of a lecture in philosophy about the humans' free will. Listening to the lecture should not evoke an enhancement of the cognitive performance in the subjects. The "control training" was parallelized in the length to the mental training.

### Assessments

The cognitive performance of participants was individually tested with the d2R (22) before and after receiving the intervention. The d2R measures attention and concentration performance within 5 min. Participants have to cancel out every "d" with two dashes in between distractors across several rows within a specific time limit. We used the measure of concentration performance of the d2R as overall measure for the participants' attention ability.

Depressive symptoms within the last 14 days were assessed with the Beck Depression Inventory II at baseline [BDI II, (23)].

The participants' ability to absorb in thoughts and imaginings was assessed with the Tellegen Absorption Scale with 34 items at baseline [TAS, (24)].

The BDI-II and the TAS were included as covariates in the data analysis.

At baseline, we also asked participants via questionnaire about some sociodemographic variables.

At the end of the assessment, participants were asked to rate (1) the effectiveness of the training and (2) what type of training the believed they received.

### Study Procedure

The investigators of the study followed a specific protocol with standardized instructions when interacting with the participants. Investigators were not blinded to the intervention and the information condition of the participants. After oral and written informed consent, participants received the BDI-II, the TAS, and a sociodemographic questionnaire. At baseline, the d2R was administered the first time. Afterwards, information about the type of training was varied according the participant's experimental condition ("You are part of our experimental condition and you will receive an effective mental training" or "You are part of our control group and you will receive the control condition"). Afterwards, participants received either the mental training or the philosophy lecture via headphones for 20 min. After listening to the audios, the participants were again tested with the d2R. After the task, they were asked to answer the previously described questions about the training they have received before. At the end of the assessment, all participants were debriefed following again a standardized protocol. The assessment took 1 h in total per participant. Subjects received either monetary compensation or got hourly credit for participating in the study.

### Statistical Analysis

We computed a three-way analysis of variance, with the betweensubjects factors intervention (mental training vs. control training) and information ("effective training" vs. "part of the control group"), and the within-subjects factor time (before and after the training). The dependent variable was cognitive performance measured before and after receiving the training. For baseline correction, we conducted an analysis of covariance with the factors intervention and information, as well as cognitive performance at baseline as covariate. Cognitive performance after the training was used as dependent variable.

### RESULTS

The four study groups were comparable at baseline regarding age, F(3, 99) = 0.21, p = 0.890, sex, X 2 (3) = 3.79, p = 0.285, the TAS, F(3, 99) = 0.56, p = 0.644, and the BDI-II, F(3, 99) = 0.41, p = 0.748.

There were differences in the four groups in the cognitive performance at baseline, almost reaching significance, F (3, 99) = 2.61, p = 0.056, see also the following analyses.

The cognitive performance significantly improved in all participants, F (1,99) = 490.01, p <0.001. Means and standard deviations are displayed in **Table 1**. We found no effect of the type of intervention, F (1, 99) = 0.11, p = 0.747, and no interaction between the factors intervention and time, F (1, 99) = 0.06, p = 0.802. Further, we found no interaction between information and time, F (1, 99) = 0.71, p = 0.402, and between information and intervention, F (1, 99) = 0.85, p = 0.358. However, we found a significant interaction between all three factors, F (1, 99) = 4.08, p = 0.046 and a significant effect of type of information, F (1, 99) = 4.79, p = 0.031. This was due to significant differences in the cognitive performance at baseline regarding the type of information, F (1, 101) = 5.72, p = 0.018. The participants that were later told to be in the control group were actually faster than those who were later instructed to receive an effective mental training ("effective mental training": M = 166.4, SD = 34.8 vs. "control group": M = 183.1, SD = 36.1).

When controlling for baseline differences in cognitive performance, there was an interaction between type of training and type of instruction, almost reaching significance, t(98) = −12.77, p = 0.063. The cognitive performance in groups with congruent information and training did not improve as much, as in groups with incongruent information (improvement "congruent": M = 33.89, SD = 20.11 vs. improvement "incongruent": M = 40.55, SD = 12.38).

The covariate depressive symptoms, assessed with the BDI-II, was not related to the cognitive performance, F (1, 96) = 0.13, p =0.723, nor was the ability to absorb, as measured with the TAS, F (1, 96) = 0.46, p =0.500.

When we compared the cognitive performance of the participants regarding their effectiveness rating at the end of the intervention, a significant interaction between time and the rating of the training was found. We observed an improvement of the cognitive performance, when the participants afterwards rated the training as neutral or effective at the end of the assessment, compared to those who rated the training as ineffective, F (2, 100) = 7.26, p = 0.001, see also **Table 2**. The improvement in cognitive performance was, however, independent of the fact if participants correctly identified the training condition or not, F (1, 101) = 1.75, p = 0.189.

The actual training they received had no significant effect on the evaluation of the effectiveness, X²(2) = 5.50, p = 0.064, see **Table 3**. The effectiveness rating at the end of the intervention was rather significantly associated with their own belief, what type of training they received, X²(2) = 10.67, p = 0.005, see **Table 4**.

These participants who rated the training as neutral or effective, showed higher scores in absorption (TAS) at baseline compared to those who rated the training as ineffective, F (2, 99) = 3.75, p = 0.027 (ineffective: M = 42.0, SD = 19.6; neutral: M = 46.4, SD = 18.3; effective: M = 56.1, SD = 25.4; post hoc Bonferroni: effective vs. ineffective: p = 0.038). No differences were found regarding age, depressive symptoms, and sex.

TABLE 1 | Cognitive performance before and after the intervention in all four experimental conditions.

M, mean; SD, standard deviation; n, sample size.

TABLE 2 | Cognitive performance before and after the intervention regarding effectiveness ratings.

M, mean; SD, standard deviation; n, sample size.

n, sample size, X2 (2) = 5.50, p = 0.064.

TABLE 4 | Effectiveness rating in the two assumed intervention conditions.

n, sample size, X2 (2) = 10.67, p = 0.005.

### DISCUSSION

Contrary to our hypothesis, that a mental training, which is only based on verbal suggestions, or the information about the effectiveness of the training could enhance cognitive performance, there was no effect of the training and the information about the training on their actual performance. Overall, we found that the cognitive performance of all participants improved. This result might be due to practicing or an effect of repeated measures [see also (22)]. However, the participant's own rating about the effectiveness of the training was significantly influenced by the cognitive performance change irrespective of the actual type of intervention or information they received. Our results suggest that it was either the perception of their own performance improvement that influenced their rating about the effectiveness at the end of the assessment. The effectiveness rating, however, was independent of the actual training they received and also of the fact if they correctly identified the training condition. Thus, another interpretation of the results could be that the subjective evaluation influenced the participant's performance in the second trial. Unfortunately, we did not assess expectations regarding the mental training and its influence on cognitive performance before the assessment.

Mental practice is known to enhance performance in general, because it involves training of specific behaviors, especially in cognitive tasks (25). Another study found that mental practicing imagining a specific motor activity—could enhance the outcome in that specific motor task (26). This finding could be interpreted as a top-down mechanism that somehow activated the brain regions that are also associated with the concrete task and thus enhance performance. Similarly, if a mental training is able to activate areas that are associated with cognitive performance, the performance itself can be improved. However, the mental practice should be regularly trained for maintaining effects (25). In our study, participants received only one session of mental training. Furthermore, several cognitive abilities are needed for assessing attention performance in a specific task like the d2R that was used in our study, for example performance speed,

accuracy, inhibition of distractors etc. (22). It might be possible that our mental training was not able to activate the specific abilities that were necessary for the attention task that we measured. Our training, which consisted of suggestions that might indirectly influence their performance, did not include any mental practice of the specific attention task. However, some higher order cognitions, as for example self-efficacy (27) or other meta-cognitive aspects like self-regulation or motivation (28), could have been more important for the cognitive outcome that we measured. Especially in student samples, perceived self-efficacy can influence the cognitive performance (29). The finding of another study, that verbal suggestions could enhance creativity, was explained by the idea that it was driven by intrinsic motivation and the belief in the own competence of the participant (30). If we transfer that explanation to our results, we could hypothesize that the participant's own motivation and belief in their performance had the biggest effect on their actual performance regardless of the information given by the investigator or the suggestions that were used in the mental training. Their own evaluation of the effectiveness of the training was consequently not based on external information but on their own intrinsic standards. The participants' motivation to improve or their perceived self-efficacy therefore influenced their performance the most. Our results are also in line with previous findings that it was rather the subjective evaluation than the objective performance that was influenced by verbal suggestions [see (7)]. The (almost significant) result that the cognitive performance improved more when subjects were given information about the type of training that was not congruent to the actual training they received, is extremely interesting within the previously discussed explanation. We interpret that result in the way that the participants' motivation to improve was even triggered more when receiving incongruent information.

We found that participants who rated the training as effective had higher hypnotic suggestibility than those who rated the training as ineffective. The effectiveness rating, however, was significantly influenced by the intervention they perceived they have received rather than the actual intervention condition that they received. This potential placebo effect implies that highly suggestible subjects might base their expectations on the owns appraisal instead of external information. We argue that the effect of enhancing cognitive performance was more pronounced in a subgroup of participants with high intrinsic motivation, high selfefficacy, and high suggestible ability. Similarly, patients with high suggestibility suffering from depression showed greater responses to suggestions and expectations regarding the effects and side effects they perceived together with taking an antidepressant medication (31). The ability to absorb in images, also known as hypnotic suggestibility [see (24)], might therefore mediate the effect of expectations on outcome [see also (31)]. However, the ability to absorb in our study had no impact on the cognitive performance itself but on the participants' own evaluation of the effectiveness of the treatment. This underlines the importance of tailoring interventions to some of the participants' characteristics or needs. Personalized medicine, also used in the psychiatric context, is based on that idea of optimizing

the fit between patient characteristics and treatment choice and therefore enhancing treatment outcome and benefit [e.g., (32)]. Furthermore, interventions that are based on hypnotic verbal suggestions should have the goal of increasing the selfefficacy and the belief in the own competence (33). This idea can be underlined by the findings regarding the influence of non-specific/common factors on the outcome of psychotherapy (34).

Placebo effects on cognitive performances were found when participants suffer from mild cognitive or attentional deficits as for example in some nicotine-smokers that were deprived before (35). Some patients with Major Depression also suffer from a cognitive impairment [see (36)], and attention or concentration problems are also included in the list of typical symptoms and criteria of depression. Mental trainings and other psychological interventions for enhancing cognitive performance might even be more effective for these patients compared to healthy academically high performers like university students. This is in line with a study that found that older adults might also profit in their cognitive performance after receiving some kind of cognitive training (37). Future studies should evaluate the effects of a mental training that focuses on cognitive enhancement especially in patients with Major Depression. Within this context, the influence of placebo effects on the cognitive performance should also be investigated.

### LIMITATIONS

There are several factors that limit the generalizability of the current study.

One limitation of the current study is that we did not conduct any pilot study to figure out if the mental training that we conceptualized was effective or not. We also did not obtain any feedback about the quality of the mental training from the participants. However, we have to note, that it was not our goal to evaluate the mental training. In contrast, we were more interested in differentiating the effects of direct suggestions and information that were given by the investigators compared to creating some images (within the mental training) that might indirectly influence the participants' performance. However, the mental training should have been evaluated in different samples regarding its effectiveness on enhancing cognitive performance. For this purpose, a full deceptive placebo design could be used. In summary, our mental training was not specifically effective for the cognitive performance in the student sample.

Second, our study sample was not representative. We measured a very young and highly educated student sample. Comparing the means of the present sample with the norms of the d2R, it was obvious that even at baseline the student sample showed an extremely high concentration performance [norms of the d2R at the age of 20–39: M = 158.6, SD = 29.4, see (22); current sample: M = 174.38, SD = 36.24]. This might be based on motivation differences regarding the assessment or some previous experience in the task [see also (22)].

We found differences in the cognitive performance of participants at baseline regarding the factor type of information. The differences were found at baseline where the instruction were not yet given to the subject. Thus, we might have created an investigator's effect. Even if the participants were randomly assigned to the experimental condition, the investigator was not blind regarding the intervention and information condition that the subjects received when interacting with him or her. Especially when the investigator knew the fact that the participant will be later told to receive the control condition, it might have been that he or she behaved in a different way when interacting with the participant that may have influenced and increased their performance. We wanted to avoid any influence of the investigator on the subject by using a standardized protocol for instructing the subjects. But maybe they were already influencing the subjects' performance unconsciously or via indirect communication. In sum, a potential investigators' allegiance effect may have confounded the results [see also (38)]. Future studies should either avoid investigator effects by blinding the investigator who is interacting with the participants regarding the type of training they receive. Another possibility could also be to directly manipulate and vary of some aspects of the contact with the participants. For example, placebo effects were enhanced when a practitioner contact was longer and focused more on the nature and history of symptom assessment compared to a relationship with only limited contact (39) and a warm empathic contact with a clinician could even result in subjective and objective ratings of improvement of cold duration and severity (40).

### CONCLUSIONS

The participants' own evaluation of the effectiveness of the training was most probably driven by their own performance in the first and second trial of the task or by their own motivation to perform. The own experiences and ratings were subsequently more important for their cognitive performance than the efficacy of a specific training or information about the training they receive. This finding underlines the relevance of enhancing the self-efficacy in situations where cognitive attention processes are important and of individually tailoring psychological trainings or interventions accordingly. The relevance of mental trainings for people with psychological disorders with a mild cognitive impairment as for example in patients with mild to moderate Major Depression Episodes should be investigated in future studies. Within this context, especially the participant's belief in the efficacy of a specific treatment should enhance their actual treatment response. The ability to absorb in images, also known as hypnotic suggestibility [see (24)], might mediate the effect of expectations on outcome and should be investigated in future psychotherapy studies.

### DATA AVAILABILITY STATEMENT

The raw data supporting the conclusions of this manuscript will be made available by the authors, without undue reservation, to any qualified researcher.

### AUTHOR CONTRIBUTIONS

Both authors contributed to the conception and design of the study. KF wrote the first draft of the manuscript. KF and DW conducted the statistical analysis. Both authors approved the submitted version.

#### FUNDING

The study was funded by the University Program for the Promotion of Junior Researchers at the Eberhard Karls

#### REFERENCES

Universität of Tübingen, awarded to KF, between July 2016 to December 2017. We acknowledge support from Deutsche Forschungsgemeinschaft and Open Access Publishing Fund of University of Tuebingen.

#### ACKNOWLEDGMENTS

We want to thank our investigators Neele Alberts, Lia Heubner, Isabell Kunze, and Tina Lorenz for helping with the data acquisition.

in patients with irritable bowel syndrome. BMJ (2008) 336:999–1003. doi: 10.1136/bmj.39524.439618.25

40. Rakel DP, Hoeft TJ, Barrett BP, Chewning BA, Craig BM, Niu M. Practitioner empathy and the duration of the common cold. Fam Med. (2009) 41:494–501.

**Conflict of Interest Statement:** The authors declare that the research was conducted in the absence of any commercial or financial relationships that could be construed as a potential conflict of interest.

Copyright © 2018 Fuhr and Werle. This is an open-access article distributed under the terms of the Creative Commons Attribution License (CC BY). The use, distribution or reproduction in other forums is permitted, provided the original author(s) and the copyright owner(s) are credited and that the original publication in this journal is cited, in accordance with accepted academic practice. No use, distribution or reproduction is permitted which does not comply with these terms.

# Effects of Placebo Interventions on Subjective and Objective Markers of Appetite–A Randomized Controlled Trial

Verena Hoffmann1 \*, Marina Lanz 1 , Jennifer Mackert 1 , Timo Müller 2,3, Matthias Tschöp2,3 and Karin Meissner 1,4 \*

1 Institute of Medical Psychology, Faculty of Medicine, LMU Munich, Munich, Germany, 2 Helmholtz Diabetes Center, Helmholtz Zentrum München, German Research Center for Environmental Health (GmbH), Munich, Germany, 3 German Center for Diabetes Research (DZD), Garching bei München, Germany, 4 Division of Health Promotion, Coburg University of Applied Sciences, Coburg, Germany

Objective: Patients' expectations about the benefit of an intervention are important determinants of the placebo effect. Little is known about the extent to which expectations influence outcomes of treatments in the field of appetite regulation. This study aimed to investigate the effects of treatment-related expectations on subjective and objective markers of appetite.

#### Edited by:

Paul Enck, University of Tubingen, Germany

#### Reviewed by:

Kristina Fuhr, University of Tubingen, Germany Damien Finniss, University of Sydney, Australia Teodora Pribic, Vall d'Hebron Research Institute (VHIR), Spain

#### \*Correspondence:

Verena Hoffmann<EMAIL_ADDRESS>Karin Meissner<EMAIL_ADDRESS>
#### Specialty section:

This article was submitted to Psychosomatic Medicine, a section of the journal Frontiers in Psychiatry

Received: 14 October 2018 Accepted: 03 December 2018 Published: 18 December 2018

#### Citation:

Hoffmann V, Lanz M, Mackert J, Müller T, Tschöp M and Meissner K (2018) Effects of Placebo Interventions on Subjective and Objective Markers of Appetite–A Randomized Controlled Trial. Front. Psychiatry 9:706. doi: 10.3389/fpsyt.2018.00706 Methods: 90 healthy participants of normal weight were randomly allocated to either an appetite-enhancing placebo group, a satiety-enhancing placebo group, or a control group. All participants received a placebo capsule along with group-specific verbal suggestions to either be appetite-promoting, or satiety-enhancing, or to have no effect on appetite. Before and during the 2 h following randomization, participants were repeatedly asked to rate feelings of hunger and satiety on visual analog scales (VAS), and blood samples were taken repeatedly to assess plasma ghrelin levels as a physiological marker of hunger.

Results: In comparison to the control group, the satiety-enhancing placebo intervention significantly reduced appetite and increased satiety. The appetite-enhancing placebo intervention did not alter subjective levels of hunger, but increased plasma ghrelin levels in females.

Conclusions: Results provide the first experimental evidence that appetite-regulating placebo interventions can elicit a psychobiological response. Expectations are important factors to consider when evaluating the effects of interventions in the field of appetite regulation.

Keywords: placebo effect, expectation, appetite, satiety, ghrelin

## INTRODUCTION

Obesity is a dramatically increasing problem in our society. Treatment approaches for obesity include psychological, pharmacological, and surgical interventions (1–3). To what extent placebo effects, i.e. positive treatment expectations, contribute to the success of obesity treatments is unclear. A recent systematic review of placebo-controlled surgery trials revealed that patients

receiving sham bariatric surgery showed on average 71% of the weight loss reported by the patients in the active surgery groups (4). These data suggest a strong inhibitory effect of placebo interventions on appetite.

Eating behavior is closely linked to mental sets. For example, Higgs (5) reported that participants consumed less in a test session when they were reminded of a recent meal. Furthermore, Provencher et al. (6) showed that participants ate less when the meal was perceived as healthy. Crum and colleagues went one step further and evaluated the impact of expectations on plasma levels of the gut hormone ghrelin, a physiological marker of appetite (7). In a within-subjects design, healthy volunteers on two occasions were made believe to receive either a "highcaloric, indulgent milk shake" or a "low-caloric, sensitive milk shake." In truth, both milk shakes were of identical contents. Results showed a different ghrelin response to these milk shakes: In comparison to the "sensible" shake, the ghrelin increase was larger when expecting the "indulgent" milk shake, followed by a sharper decline of ghrelin levels 30 min after drinking the shake. These findings indicate a strong impact of nutrition-specific expectations on appetite and satiety, as evidenced by altered plasma ghrelin levels before and after a test meal. Additionally, differences in eating behavior are linked to gender. Several studies have shown that females tend to eat healthier than men [i.e., avoiding high-fat food and eating more fruit and fiber; (8, 9)]. This has been linked to more concerns of women about their body weight as compared to men (10). Also, it has been reported, that females eat more sweets when perceiving stress than men (11).

In this study, we investigated whether treatment-related expectations can affect appetite, satiety and plasma ghrelin levels. In a between-subjects design, normal-weight participants received a placebo capsule together with the information that its content would either increase appetite, or increase satiety, or would leave appetite and satiety unaffected. We hypothesized that the appetite-enhancing placebo intervention would decrease satiety and increase appetite and plasma ghrelin levels, while the satiety-enhancing placebo intervention would have the opposite effects, both in comparison to a no treatment control group.

## MATERIALS AND METHODS

#### Participants

The study was conducted at the Institute of Medical Psychology at the LMU Munich, Germany. Healthy participants aged 18–36 years were recruited via flyers and a university mailing list. All participants had to be of normal weight (Body Mass Index (BMI) 18–25 kg/m2 ). Exclusion criteria included report of pregnancy, breastfeeding, regular use of medication (except hormonal contraceptives and anti-allergic drugs), acute or chronic disease, smoking, surgery in the last 4 weeks before the experiment, elevated fasting blood glucose levels (>100 mg/dl), and elevated levels of anxiety and/or depression scores [>7 in at least one subscale of the Hospital Anxiety and Depression Scale (HADS); (12)]. The study protocol was approved by the ethics committee of the Medical Faculty at LMU Munich. Participants provided written informed consent and received 45 Euro compensation.

### Experimental Procedure

Ninty participants were randomly allocated to one of three groups: "control," "enhanced appetite" (placebo), or "enhanced satiety" (placebo). To allow for double-blinding, 6 additional participants were randomized to verum treatments (3 enhanced appetite, 3 enhanced satiety; compare (13); **Figure 1**).  At recruitment, participants were informed that the experiment investigated how biological and psychological factors contribute to the regulation of hunger and appetite.

Participants underwent a single test session starting at 8 o'clock in the morning. They were asked to abstain from food for 10–12 h prior to the experiment (intake of small amounts of water was allowed). Upon arrival, participants took seat in a comfortable chair, and blood glucose levels were determined from finger blood samples using a BG Star device (Sanofi-Aventis, Hannover, Germany). An indwelling flexible catheter was then placed in the antecubital vein and kept patent with a saline infusion to allow for repeated blood drawing during the experiment. Electrodes to measure the electrocardiogram (ECG) were attached. Participants were then asked to fill in the "Hospital Anxiety and Depression Scale" [HADS; (12)], the 'Three Factor Eating Questionnaire' [TFEQ; (16)] and to rate current levels of hunger and satiety on 100-mm visual analog scales (VAS). Thereafter, the first blood sample to assess ghrelin levels was collected and the ECG measurement was started. Following a 15-min baseline period, the experimenter opened the randomization envelope, performed the verbal expectancy manipulation according to group allocation ("appetite increase," "satiety increase," or "control") and asked the participants to swallow the provided test capsule with 100 ml of mineral water (standardized temperature of 20◦C). After resting periods of 30 and 60 min, respectively, participants were asked to rate current levels of hunger and satiety, and the second and third blood sample for ghrelin assessments were collected.

### Blinding and Randomization

A person not directly involved in the experiments prepared an opaque, sequentially-numbered randomization envelope for each participant according to a computer-generated randomization list. The envelopes contained information on the type of intervention ("appetite-stimulating," "satiety-enhancing," or "control") as well as a test capsule. Neither the experimenter nor the participants were informed whether the capsule in the hunger-enhancing and satiety-enhancing conditions was a placebo or contained an active ingredient (double-blinded design).

### Capsules

Identical white and opaque vegetarian capsules were used for all interventions. The placebo capsules were filled with lactose (Heirler Cenovis GmbH, Radolfzell, Germany). For the satietyincreasing active intervention, capsules were filled with an alginate complex (lyophilized sodium-alginate complex, added with aluminum- and calciumchoride; CM3 Alginat Kapseln, Easyway GmbH, Monheim, Germany). Alginate reduces hunger

and increases satiety feelings, which is partly due to its volumeincreasing content (17). For the appetite-stimulating active intervention, one tablet of "Appetit-Anreger" with extracts of bitter herbs (Zirkulin Naturheilmittel GmbH, Bremen) was placed in the study capsules. Dietary supplements containing bitters are traditionally used to increase appetite and to support digestion (18).

enhanced satiety"). The verum groups served only for double-blinding and were not evaluated further.

### Expectancy Manipulation

Standardized expectancy manipulations were performed by two female experimenters in white coats (one undergraduate, one graduate student). After opening the randomization envelopes, participants in the appetite-stimulating groups were told to receive either a placebo capsule or a capsule filled with bitters, and that bitters are known to increase secretion of digestive fluids in the stomach and thus are expected to increase appetite within 20–30 min after intake of the capsule. Participants in the satiety-enhancing groups were told to receive either a placebo capsule or a capsule containing alginate, and that alginate is known to increase its volume in the stomach and thus is expected to enhance satiety within 20– 30 min after intake of the capsule. They were told to receive either a verum or a placebo intervention (randomization ratio was not disclosed). Participants in the control group received a placebo capsule together with the information that its ingredients would have no effect on gastric activity and appetite.

### Measurements Hunger and Satiety Ratings

Perceived hunger ("How hungry do you feel?") was rated using a 100-mm visual analog scale from "0" ("not at all hungry") to "100" ("extremely hungry"). Perceived satiety ("How full do you feel?") were assessed by means of a 100-mm visual analog rating scale, ranging from 0 ("not at all full") to 100 ("extremely full").

#### Plasma Ghrelin

To assess the concentration of ghrelin in plasma, blood samples were collected in commercially available EDTA tubes (2.7 ml), complemented with 54 µl 4 mM 4-(2 aminoethyl)benzenesulfonyl fluoride hydrochloride (AEBSF) (19). Blood samples were immediately stored on ice and centrifuged within 30 min for 10 min at 3,000 g and 4◦C. Two samples of 500 µl plasma were transferred to Eppendorf tubes and complemented with 100 µl 1 mM HCl. Samples were gently mixed and stored at −70◦C until final analysis. Analysis of plasma ghrelin content was performed with the Ghrelin (total) Assay Kit (Catalogue number: EZGRT-89K) from Merck Millipore, Darmstadt, Germany according to protocol.

#### Electrocardiogram

The electrocardiogram was recorded to evaluate changes in heart rate. A transient increase of heart rate has been described as part of the cephalic phase response when food is anticipated (20). The electrocardiogram signal was measured continuously during the experiment using three disposable Ag/AgCl electrodes, which were positioned in an Einthoven Lead I configuration and connected to the BIOPAC amplifier module ECG100C of a BIOPAC MP 150 device (BIOPAC Systems Inc., Goleta, CA, USA). Data was acquired using AcqKnowledge 3.7.2 software and a sampling rate of 500 Hz. Intervals between successive R peaks (cardiac periods) were extracted from the electrocardiogram signal using the peak-detection function implemented in AcqKnowledge 3.7.2. Heart periods were examined and screened for artifacts based on the procedure developed by Proges and Byrne (21). Average heart rate was calculated for the last five artifact-free minutes of the baseline period and the two postintervention periods (i.e., minutes 25–30 and minutes 55–60 after randomization).

#### Questionnaires

The Hospital Anxiety and Depression scale [HADS; (12)] was used to screen for anxiety and/or depression. The Three Factor Eating Questionnaire [TFEQ; (16)] with its three subscales "cognitive restraint of eating," "disinhibition," and "hunger" was used to test for possible differences in eating behavior between groups at baseline.

Female participants were asked for the normal length of their menstrual cycle, the beginning of the last menstruation, and whether they took hormonal contraceptives. Time point of ovulation was estimated by subtracting 14 days from the length of the menstrual cycle (22).

#### Statistical Analyses

Assuming an effect size partial eta-squared of 0.1, the study was planned to have a power of 90% to detect a significant interaction effect between "group" and "time point" in a mixed ANOVA for changes of hunger, satiety and ghrelin from before to after the intervention (with a type 1 error of 5%) (calculated by GPower Version 3.1.7). However, we later decided to use ANCOVAs to adjust for the slight group differences at baseline. Statistical analyses were performed using SPSS (version 23.0). Hunger ratings, satiety ratings and plasma ghrelin levels were each subjected to 3-way analyses of covariance (ANCOVA), with

TABLE 1 | Group characteristics at baseline.

two levels of "time" (30 min and 60 min after randomization), three levels of "group" (appetite, satiety, control) and two levels of "sex" (male, female). In each model, baseline levels (15 min before randomization) were included as covariates. Bonferroni corrections were applied, where appropriate. A p-value ≤ 0.05 (2-sided) was considered statistically significant.

### RESULTS

#### Participants

One Hundred thirteen participants were assessed for eligibility and 17 were excluded (three did not meet inclusion criteria, 12 declined to participate, one did not show up and one had elevated fasting blood glucose levels). Thirty participants each were assigned to the appetite group, the satiety group, and the control group. All participants completed the experiment.

Study groups were comparable with respect to demographic variables, eating behavior as well as anxiety and depression scores (**Table 1**). Participants had a mean age of 26.6 years (3.2 SD; range: 18–36 years) and a mean BMI of 21.9 kg/m2 (1.8 SD; range: 18.6–25 kg/m2 ). Fourteen women were in the preovulatory phase and two women in the postovulatory phase of the menstrual cycle, while 29 women were using hormonal contraceptives.

#### Hunger Ratings

The 3-way ANCOVA for post-intervention hunger ratings, controlled for baseline levels, revealed a significant 3 way interaction between "group," "time," and "sex" [Fgroup×time×sex(2, 83) = 4.0, p = 0.023]. However, post hoc 2-way ANCOVAs performed separately for each sex showed no significant interaction effect between "group" and "time" [women, Fgroup×time(2, 41) = 3.1, p = 0.058; men, Fgroup×time(2, 41) = 0.6, p = 0.571). Furthermore, the 3-way ANCOVA showed a significant main effect of "group" [Fgroup (2, 83) = 6.7, p = 0.002]. Bonferroni-corrected post hoc tests indicated significantly lower hunger ratings in the satiety group compared to the control group (p = 0.033) and to the appetite group (p = 0.002) (**Figure 2**, **Table 2**).

SD, Standard Deviation.

#### Satiety Ratings

The 3-way ANCOVA for post-intervention satiety ratings, controlled for baseline levels, revealed a significant main effect of "group" [F(2, 83) = 11.1, p < 0.001]. Bonferroni-corrected post hoc tests indicated significantly higher satiety ratings in the satiety group than in the control group (p < 0.001) and in the appetite group (p < 0.001) (**Figure 3**, **Table 2**). The 3-way interaction between "group," "time," and "sex" was not significant [Fgroup×time×sex(2, 83) = 2.5, p = 0.102].

#### Ghrelin Levels

The 3-way ANCOVA for post-intervention plasma ghrelin levels, controlled for baseline levels, revealed a significant 2-way interaction between "group" and "sex" [F(2, 71) = 3.4, p = 0.040]. Separate ANCOVAs for male and female participants indicated a significant main effect of "group" in women [F(2,37) = 4.4, p = 0.019] but not in men [F(2, 33) = 1.5, p = 0.235]. Bonferronicorrected post hoc tests indicated that the interaction in women was due to higher post-intervention ghrelin levels in the appetite group compared to the control group (p = 0.019; **Figure 4**, **Table 2**). Neither the main effect of "group" [Fgroup(2, 71) = 0.9, p = 0.401) nor the 3-way interaction between "group," "time," and "sex" [Fgroup×time×sex(2, 71) = 2.7, p = 0.075] was significant.

### Heart Rate

The 3-way ANCOVA for post-intervention heart rate, controlled for baseline levels, revealed no significant main or interaction

#### Treatment Guesses

Thirteen participants (72.2%) in the satiety group, but only five participants (27.8%) in the appetite group guessed to having received the active agent. The difference between groups was significant (χ² = 0.1, p = 0.024).

### DISCUSSION

This is the first study designed to evaluate the effects of treatment-related expectations on appetite, satiety, and associated plasma ghrelin levels. Our randomized-controlled double-blinded experiment revealed that the satiety-enhancing placebo intervention successfully altered subjective feelings of appetite and satiety in the suggested direction. Furthermore, the appetite-enhancing placebo intervention increased ghrelin levels in women.

A recent meta-analysis of sham-controlled surgery trials suggested that bariatric surgery for obesity is associated with a large placebo effect on weight loss, equaling 71% of the effect of active bariatric surgery (4). Our finding that the satiety-enhancing placebo intervention indeed increased satiety provides the first experimental evidence that treatment-related expectations contribute to the success of satiety-enhancing medical interventions.

TABLE 2 | Post-intervention values (baseline-adjusted) of hunger ratings, satiety ratings, plasma ghrelin levels, and heart rate.

SE, Standard Error; VAS, Visual Analogue Scale.

The retrospective evaluation of treatment guesses suggests that the appetite-enhancing placebo intervention was less credible to the participants than the satiety-enhancing placebo intervention. This could explain why the appetite-enhancing placebo intervention did not alter subjective feelings of appetite and satiety. However, the guess of having received placebo does not necessarily mean that the participant did not believe in the effectiveness of the intervention. Recent studies indicate that also open-label placebo administration can lead to positive beliefs and symptom improvement (23–25). Supporting this explanation, we observed an increase in ghrelin levels following the appetiteenhancing placebo intervention in women, suggesting the occurrence of a placebo effect on a physiological level. Ghrelin is secreted by the stomach, with levels peaking just before a meal and declining after feeding. In addition, ghrelin serves as an interoceptive signal for food-seeking behavior (26, 27). A previous study in a predominantly female cohort (65% women) found that plasma ghrelin levels increased when participants anticipated the intake of an "indulgent" milk-shake as compared to a "low-calorie" milk-shake, even though hunger ratings did not change (7). This may indicate that ghrelin is a highly sensitive measure to capture a psychologically mediated increase in appetite that occurs even before behavioral effects are measureable. With regard to the observed sex difference, it is important to note that stronger physiological placebo responses in women have also been reported in studies of placebo analgesia (15, 28). In addition, there is ample evidence that the physiology of appetite differs between sexes (29, 30). For example, women showed higher brain activation in the fusiform gyrus while viewing high-caloric pictures in the hungry state (31). Furthermore, brain activation to calorie-rich foods within the dorsolateral, ventrolateral, and ventromedial prefrontal cortices, the middle/posterior cingulate, and the insula were larger in women than in men (32), regions that play a role in selfreflection (33). Interestingly, sex differences in eating behavior are mediated, among other factors, by the gut hormone ghrelin (14), both in terms of secretion of this hormone and of ghrelin sensitivity (34, 35). Thus, the sex-specific ghrelin response in our experiment is in line with previous studies showing a stronger physiological response to placebo interventions as well as to appetite-enhancing food stimuli in women.

Our results provide first evidence that a placebo intervention to enhance appetite may enhance ghrelin secretion in women even before behavioral effects are measureable. In contrast, we found a strong effect of the satiety-enhancing intervention on ratings of hunger and satiety, notably without changes in circulating levels of total ghrelin. These data collectively suggest that ghrelin secretion is most likely unrelated to the placebo effect on satiety. It could be argued that food ingestion is a prerequisite for the postprandial fall in circulating ghrelin. However, as demonstrated in healthy human volunteers, postprandial suppression of ghrelin secretion did not differ between subjects receiving a mixed meal or who have been sham fed to allow smelling, chewing and tasting but not swallowing of food (26, 36). An anorexigenic hormone such as leptin or peptide YY (37) may still be better suited to capture the hormonal correlates of the placebo effect on satiety.

Several limitations of our results need to be mentioned. First, the short observational period in our experiment does not allow any conclusion on whether placebo effects on hunger and satiety can last longer than a few hours. Second, we performed our experiment in a normal-weight sample. Further studies are needed to clarify whether the findings of our experiment can be replicated in obese and anorectic patients. Third, our study was designed to investigate placebo effects on hunger and satiety induced by verbal suggestions. Learning mechanisms, such as behavioral conditioning and reinforcement learning, are known to affect eating behavior (38) as well as placebo effects (39), and their involvement in placebo effects on appetite-regulation should be evaluated in follow-up studies.

In conclusion, the results of the present study indicate a powerful inhibition of appetite in response to a satiety-enhancing placebo intervention and first evidence for an increase of ghrelin levels in women in response to an appetite-enhancing placebo intervention. Results thus provide the first experimental evidence that expectations are important factors to consider when evaluating the effects of medical interventions in the field of appetite regulation. Further studies with additional physiological outcome parameters are needed to better understand the psychobiological processes triggered by appetite-modulating placebo interventions.

#### AUTHOR CONTRIBUTIONS

VH and KM designed the experiments. VH, ML and JM performed the experiments. VH and KM analyzed the data. VH, TM, MT, and KM interpreted the data. VH drafted the first version of the manuscript. All authors critically reviewed the manuscript.

#### ACKNOWLEDGMENTS

KM received support by the Theophrastus Foundation, Germany, the Schweizer-Arau Foundation, Germany, and KM and MT by the Deutsche Forschungsgemeinschaft (ME-3675/1-1).

### REFERENCES

**Conflict of Interest Statement:** The authors declare that the research was conducted in the absence of any commercial or financial relationships that could be construed as a potential conflict of interest.

Copyright © 2018 Hoffmann, Lanz, Mackert, Müller, Tschöp and Meissner. This is an open-access article distributed under the terms of the Creative Commons Attribution License (CC BY). The use, distribution or reproduction in other forums is permitted, provided the original author(s) and the copyright owner(s) are credited and that the original publication in this journal is cited, in accordance with accepted academic practice. No use, distribution or reproduction is permitted which does not comply with these terms.

# The Influence of Expectancy Level and Personal Characteristics on Placebo Effects: Psychological Underpinnings

Lili Zhou1,2, Hua Wei 3 , Huijuan Zhang1,2, Xiaoyun Li 3 , Cunju Bo4 , Li Wan4 \*, Xuejing Lu1,2 \* and Li Hu1,2,3,4

*1 CAS Key Laboratory of Mental Health, Institute of Psychology, Chinese Academy of Sciences, Beijing, China, 2 Department of Psychology, University of Chinese Academy of Sciences, Beijing, China, 3 Key Laboratory of Cognition and Personality, Ministry of Education, Faculty of Psychology, Southwest University, Chongqing, China, 4 Department of Pain Management, The State Key Clinical Specialty in Pain Medicine, The Second Affiliated Hospital of Guangzhou Medical University, Guangzhou, China*

#### Edited by:

*Luana Colloca, University of Maryland, Baltimore, United States*

#### Reviewed by:

*Meike C. Shedden-Mora, University Medical Center Hamburg-Eppendorf, Germany Karin Meissner, Ludwig Maximilian University of Munich, Germany*

#### \*Correspondence:

*Xuejing Lu<EMAIL_ADDRESS>Li Wan<EMAIL_ADDRESS>
#### Specialty section:

*This article was submitted to Psychosomatic Medicine, a section of the journal Frontiers in Psychiatry*

Received: *30 April 2018* Accepted: *11 January 2019* Published: *05 February 2019*

#### Citation:

*Zhou L, Wei H, Zhang H, Li X, Bo C, Wan L, Lu X and Hu L (2019) The Influence of Expectancy Level and Personal Characteristics on Placebo Effects: Psychological Underpinnings. Front. Psychiatry 10:20. doi: 10.3389/fpsyt.2019.00020* Placebo effects benefit a wide range of clinical practice, which can be profoundly influenced by expectancy level and personal characteristics. However, research on the issue of whether these factors independently or interdependently affect the placebo effects is still in its infancy. Here, we adopted a 3-day between-subject placebo analgesia paradigm (2-day conditioning and 1-day test) to investigate the influence of expectancy levels (i.e., No, Low, and High) and personal characteristics (i.e., gender, dispositional optimism, and anxiety state) on placebo effects in 120 healthy participants (60 females). Our results showed that the reduction of pain intensity in the test phase was influenced by the interaction between expectancy and gender, as mainly reflected by greater reductions of pain intensity in females at Low expectancy level than females at No/High expectancy levels, and greater reductions of pain intensity in males than in females at High expectancy level. Additionally, the reduction of pain unpleasantness was not only modulated by the interaction between expectancy and gender, but also by the interaction between expectancy and dispositional optimism, as well as the interaction between expectancy and anxiety state. Specifically, participants who were more optimistic in Low expectancy group, or those who were less anxious in High expectancy group showed greater reductions of pain unpleasantness. To sum up, we emphasized on regulating the expectancy level individually based on the assessment of personal characteristics to maximize placebo effects in clinical conditions.

Keywords: expectancy, placebo analgesia, gender, dispositional optimism, anxiety state

## INTRODUCTION

Placebo commonly refers to an inert substance or a medicinally inactive treatment that can generate clinically-useful effects. A person who receives a placebo treatment usually experiences actual improvements in his/her physical condition, which is well-known as the placebo effect. The placebo effect can be beneficial in a wide range of clinical situations, such as modulating the therapeutic effects of deep brain stimulation on Parkinson's disease, generating antidepressant responses in depression, and reducing unpleasantness in patients with anxiety (1, 2). It can also enhance the

effectiveness of physical interventions (3–5) and provide an alternative approach to avoid side effects of drug treatments (6, 7).

Although placebo effect is a complex phenomenon that can be affected by multiple factors (e.g., memory, motivation, anxiety, learning, patient-provider interaction, and previous treatment experience) (1, 8–10), response expectancy has been recognized as one of the main psychological mechanisms underlying this effect (11). Response expectancy has been defined as the expectancy to the occurrence of non-volitional responses (i.e., responses experienced as occurring automatically without volitional efforts, including fear, sadness, sexual arousal, pain, etc.) to situational cues (12). According to Response Expectancy Theory, such response expectancy could affect the probability that an individual would engage in a particular behavior (e.g., increased/decreased pain responses), as non-volitional responses have positive and negative reinforcement values (12). Consistent with this theory, accumulating evidence has shown that the placebo effect (e.g., placebo analgesia) could be altered by changing individual expectancy (3, 7, 13–19).

In general, response expectancy is composed of two distinct aspects: (1) the expected magnitude of a change (i.e., expectancy level), and (2) the subjective probability that the change will occur (i.e., individual belief) (12). With regards to the first aspect of response expectancy, a greater placebo effect is usually associated with a higher level of positive expectancy (4, 5, 20–23). However, these observations are not guaranteed under some circumstances. For example, in laboratory settings, even individual expectation of placebo effects has been successfully acquired during the classical conditioning phase, unrealistically high expectancy that does not match with one's present experience would weaken individual belief in the placebo treatment during the test phase (24).

In terms of the second aspect of response expectancy, previous studies have demonstrated that individual belief in the current experience has a critical influence on response expectancy through learning mechanisms (21, 24). Such a belief is easily affected by personal characteristics, thus contributing to the differentiation of individual expectancy (25, 26), and subsequently leading to individual variability in response to placebos (27, 28). For instance, gender has been verified as a factor contributing to the variability of placebo effects—some studies suggested that males reported greater pain reductions after placebo treatments compared to females (29–31), whereas other studies described a better respondence to placebos in females than in males (29, 32–34). Additionally, the influence of other personal characteristics on placebo responses has been frequently reported in the literature. For example, dispositional optimism, referred to a generalized positive outcome expectancy for the future (35), is inextricably linked to proneness of increased placebo effects (36, 37). Comparatively, individuals with low anxiety level are more likely to respond to a placebo treatment (36).

However, research on the issue of whether expectancy level and personal characteristics independently or interdependently affect the placebo effects is still in its infancy. Here, we adopted a between-subject placebo analgesia paradigm to test the influence of expectancy levels (i.e., No, Low, and High) and personal characteristics (i.e., gender, dispositional optimism, and anxiety state) on placebo effects.

### MATERIALS AND METHODS

### Participants

A total of 120 healthy, right-handed participants (60 females) were recruited from the local community. None of them reported a history of illness or concurrent medication. Participants were informed that they were attending a study aimed to test the effect of lidocaine (a local anesthetic that could be topically applied on the skin) on alleviating pain, and they were asked not to consume products containing caffeine, alcohol, or nicotine at least 12 h before the experiment. All the participants gave their written informed consents and were told their rights to discontinue participation at any time during the study. Each participant was randomly assigned to one of the three experimental groups divided by the manipulated expectancy levels (i.e., No, Low, and High) during the Conditioning phase (as described below), with 40 participants (20 females) in each group. After the whole experiment, all participants were fully debriefed.

### Experimental Materials

#### Pain Stimuli

The electrical pain stimuli were delivered using a constantcurrent stimulator (model DS7A; Digitimer, UK) with three stainless steel concentric bipolar needle electrodes (38, 39). Pain stimuli were intraepidermal electrical pulses delivered to the inner side of the left forearm through the electrodes (located according to an equilateral triangle shape), which have been proved to preferentially activate the Aδ nociceptive fibers in the superficial skin layers (40, 41). Each electrode consisted of a needle cathode (length = 0.1 mm, diameter = 0.2 mm) surrounded by a cylindrical anode (diameter = 1.4 mm). Each stimulus consisted of 100 rapidly succeeding constantcurrent, square-wave pulses at 50 Hz (0.5-ms duration for each pulse).

#### Dispositional Optimism

The Chinese version of the Life Orientation Test-Revised (LOT-R) was adopted to assess participants' dispositional optimism, as its reliability has been well-established (Cronbach alpha of positive subscale = 0.73, N = 479; Cronbach alpha of negative subscale = 0.82, N = 479) (42). In the current sample, the reliability of the scale was satisfactory (Cronbach alpha = 0.66, N = 120).

#### Anxiety State

The state subscale of Chinese version of State-Trait Anxiety Inventory (STAI-S) was adopted to assess participants' anxiety state. The reliability of the Chinese version of STAI-S (Cronbach alpha = 0.90, N = 2,150) (43) has been wellestablished. Notably, the reliability of the subscale in the current sample was satisfactory (STAI-S: Cronbach alpha = 0.89, N = 120).

### Experimental Procedure

A randomized, single-blinded between-subject experimental paradigm of placebo analgesia was adopted in the present study (7). Participants were firstly familiarized with the electrical stimulation prior to the formal experiment. The stimulus intensities were adjusted individually using the method of limits, to identify the thresholds for each participant that would elicit a low sensation (∼2 rating), moderate sensation (∼4 rating), and high sensation (∼6 rating) on an 11-point self-report Numeric Rating Scale (NRS, 0 = no sensation, 10 = unbearable pain). Specifically, the stimuli at ∼2 rating elicited a non-painful sensation, whereas the stimuli at ∼4 and ∼6 ratings elicited a painful pinprick sensation. Once these stimulus intensities were determined, a randomized sequence of pain stimuli with different intensities was delivered to participants until they were able to reliably distinguish the intensities of these stimuli. Notably, these determined stimuli with varied intensities were used during the conditioning procedure (see Conditioning Phase section) to ensure a successful manipulation of expectancy level during the experiment.

The experiment consisted of two phases in three consecutive days: Conditioning phase (Day 1 and Day 2) and Test phase (Day 3). On each day, participants underwent three sessions: (1) a pre-treatment session, (2) a treatment session, and (3) a post-treatment session (see **Figure 1**). To rule out possible confounding effects related to the gender of experimenter (44, 45), half of participants in each group with an equal number of males (n = 20) and females (n = 20) were instructed by a female experimenter, while the rest were guided by a male experimenter. Both female and male experimenter wore white coats and had received systematic training of procedure prior to the formal experiment.

#### Conditioning Phase

The Conditioning phase started with a pre-treatment session consisting of 20 trials. Each trial started with a 1 s white fixation centered on the screen with a black background. After a 5 s waiting, an electrical stimulus at ∼6 ratings (0.80 ± 0.29 mA) lasting for 2 s was delivered to the left forearm of the participant. Being waiting for another 5 s, participants were required to verbally rate the perceived intensity (0 = no sensation, 10 = unbearable pain) and unpleasantness (0 = not unpleasant, 10 = extremely unpleasant) of pain evoked by the electrical stimulus (with 8 s per each rating, 16 s in total). The inter-trial interval varied between 8 and 12 s. The stimulus intensity in the pre-treatment session was identical across groups and the whole session lasted for ∼16 min.

In the treatment session, a non-active skin cream was applied on the palmar side of the participant's left forearm. Being waiting for 5 min, participants were instructed to remove the cream and have a 10 min rest. Meanwhile, in order to strength expectancy level, participants were given one of the following verbal interventions, depending on treatment assignment:

The treatment session lasted for ∼15 min.

The Conditioning phase ended with a post-treatment session consisting of 40 trials. The procedure was identical to the pretreatment session, except that different intensities of electrical stimuli were set for different groups: inducing a painful sensation at ∼6 rating (0.69 ± 0.16 mA) for No expectancy group, at ∼4 rating (0.47 ± 0.17 mA) for Low expectancy group, and a non-painful sensation at ∼2 rating (0.28 ± 0.08 mA) for High expectancy group. Such changes of stimulus intensity for different groups were intended to strengthen the power of verbal intervention to response expectancy, which has been frequently applied in previous placeborelated studies (46–48). The post-treatment session lasted for ∼37 min.

#### Test Phase

The Test phase also consisted of a pre-treatment session, a treatment session, and a post-treatment session. The procedure of this phase was identical to the Conditioning phase, except that the intensity of electrical stimuli applied in the posttreatment session was identical for all participants across groups, i.e., inducing a painful pinprick sensation at ∼6 rating (0.78 ± 0.26 mA). Participants were first required to complete the psychological questionnaires upon arriving to the laboratory on the Test day. To make sure that the expectancy manipulation was successful, participants in the Low and High Expectancy groups were required to verbally rate the strength of expectancy to drug efficacy on an 11 point NRS (0 = without any expectancy, 10 = full expectancy) at the end of the test. The average ratings of expectancy to drug efficacy were significantly different between groups (Low: 6.90 ± 1.31, High: 8.39 ± 0.80, t = −6.11, P < 0.001), indicating a successful expectancy manipulation. For participants in No expectancy group, the expectancy to drug efficacy was not assessed to avoid extra response bias to the expectancy manipulation.

### Statistical Analysis

To assess the magnitude of placebo effects, we calculated the changes of subjective pain intensity and unpleasantness by subtracting the ratings in the post-treatment session from those in the pre-treatment session in Test phase (49). To demonstrate the influence of personal characteristics on the modulation of expectancy level on placebo effects, we performed a statistical analysis using a "split into three subgroups" strategy (13-14- 13 split). Specifically, we sorted the LOT-R scores in ascending order and split the data into low (13 participants), middle (14 participants), and high LOT-R subgroups (13 participants) for each experimental condition. Following, we performed three-way analyses of variance (ANOVAs) on the indicators

of placebo effects, with "expectancy level" (No, Low, and High), "dispositional optimism (LOT-R)" (low and high), and "gender" (female and male) as between-subject factors. Likewise, scores of anxiety state (STAI-S) were sorted and analyzed using the same statistical strategy. The statistical P-values were adjusted with Greenhouse-Geisser correction to avoid violation of the sphericity assumption, when necessary. Post hoc pairwise comparisons were performed with Bonferroni adjustments, when the main effects or interactions reach statistical significance. The effect size and statistical power in the present sample were estimated by partial eta-squared and 1-β, respectively. For partial eta-squared (η 2 p ), an effect size of 0.0099 is deemed as a "small" effect, around 0.0588 as a "medium" effect, and 0.1379 to infinity as a "large" effect (50). For 1- β, 0.8 is the commonly acceptable statistical power. To detect the effectiveness of sample size used in the current study, we performed a prior computation on the required sample size using G∗power (an online free software for power analysis, available at http://www.gpower.hhu.de/en. html) by setting statistical power at 0.8 with large effect size (η 2 p = 0.1379). The result showed a minimal sample size of 64 in total to detect the main effects and interactions between independent variables, which indicated that our sample size (N = 120) was enough to detect these effects. All statistical analyses were carried out in SPSS 22.0 statistical analysis package (SPSS Inc., New York, USA). Statistical threshold was set at 0.05.

## RESULTS

### Participant Characteristics

Participant characteristics for each experimental group are summarized in **Table 1**. The age was not significantly associated with "expectancy level" (No, Low, and High) and "gender" (female and male) [F(2,114) = 2.84, P = 0.06, η 2 p = 0.05]. This result, together with the counterbalanced experimental design for gender, indicated that all the participants across groups were ageand gender-matched, thus avoiding possible bias when assessing placebo effects.

### Influence of Expectancy Level, Dispositional Optimism, and Gender on Placebo Effects

Significant main effects of "expectancy level" [F(2,72) = 7.06, P = 0.002, ηp 2 = 0.172] and "dispositional optimism (LOT-R)" [F(1, 72) = 5.18, P = 0.026, ηp 2 = 0.071] were observed, while no significant main effect of "gender" [F(1, 114) = 0.04, P = 0.848, ηp 2 = 0.001] was showed in the reduction of pain intensity (see **Table 2**). Post hoc comparisons on "expectancy level" showed that participants in Low expectancy group elicited a greater reduction of pain intensity than both No (P < 0.001) and High (P = 0.055) expectancy groups, while the latter two had no significant difference (P = 0.29). Neither the interaction between "expectancy level" and "dispositional

*F, Female; M, Male.*

TABLE 2 | The changes of pain intensity from pre-treatment to post-treatment sessions in all experimental groups (data are expressed as M ± SD).

*F, Female; M, Male; LOT-R, Life Orientation Test-Revised; STAI-S, State subscale of State-Trait Anxiety Inventory. Changes of pain intensity were obtained by subtracting the ratings in post-treatment sessions from those in pre-treatment sessions.*

optimism (LOT-R)" [F(1, 72) = 0.79, P = 0.460, ηp 2 = 0.023] (**Figure 3**, left panel), nor the interaction between "dispositional optimism (LOT-R)" and "gender" [F(2,72) = 0.20, P = 0.655, ηp 2 = 0.003] (see **Figure 2**, left panel) was significant. However, the interaction between "expectancy level" and "gender" [F(2,114) = 4.29, P =0.018, ηp 2 = 0.112] was significant. Post-hoc comparison on this interaction revealed that (1) female participants in the Low expectancy group reported a greater reduction of pain intensity due to placebo treatment than females in No (P < 0.001) and High (P = 0.001) expectancy groups; (2) for participants in High expectancy group, males reported a greater reduction of pain intensity due to placebo treatment than females (P = 0.01).

In contrast, main effects of "expectancy level" [F(2,72) = 1.00, P = 0.374, ηp 2 = 0.029], "dispositional optimism (LOT-R)" [F(1, 72) = 0.05, P = 0.832, ηp 2 = 0.001], and "gender" [F(1, 72) = 0.03, P = 0.874, ηp 2 < 0.001] were not significant on the reduction of pain unpleasantness (see **Table 3**). Except of non-significant interaction between "dispositional optimism (LOT-R)" and "gender" [F(2,72) = 0.78, P = 0.379, ηp 2 = 0.011], both the interaction between "expectancy level" and "dispositional optimism (LOT-R)" [F(2,72) = 3.26, P = 0.044, ηp 2 = 0.084] (**Figure 3**, right panel), and the interaction between "expectancy level" and "gender" [F(2,72) = 3.38, P = 0.040, ηp 2 = 0.091] (**Figure 2**, right panel) were statistically significant. Post-hoc comparison on the interaction between "expectancy level" and "dispositional optimism (LOT-R)" showed that (1) for participants with high LOT-R scores, those in Low expectancy TABLE 3 | The changes of pain unpleasantness from pre-treatment to post-treatment sessions in all experimental groups (data are expressed as M ± SD).

*F, Female; M, Male; LOT-R, Life Orientation Test-Revised; STAI-S, State subscale of State-Trait Anxiety Inventory. Changes of pain unpleasantness were obtained by subtracting the ratings in post-treatment sessions from those in pre-treatment sessions.*

group experienced a greater reduction of unpleasantness due to placebo treatment than those in No expectancy group (P = 0.046); (2) for Low expectancy group, participants with high LOT-R scores had a tendency to report a greater reduction of unpleasantness than those with low LOT-R scores (P = 0.056; see **Table 3**). Similar to the results of pain intensity, post-hoc pairwise comparisons showed that (1) female participants in the Low expectancy group reported a greater reduction of unpleasantness due to placebo treatment than those in High expectancy group (P = 0.039); (2) for participants in High expectancy group, males tended to report a greater reduction of unpleasantness due to placebo treatment than females (P = 0.073).

### Influence of Expectancy Level, Anxiety State, and Gender on Placebo Effects

For the reduction of pain intensity, there was a significant main effect of "expectancy level" [F(2, 72) = 4.14, P = 0.02, ηp 2 = 0.026]. Post-hoc comparisons showed that participants in Low expectancy group reported a greater reduction of pain intensity than those in No expectancy group (P = 0.007). No significant main effect of "gender" [F(1, 72) = 3.07, P = 0.082, ηp 2 = 0.09] or "anxiety state (STAI-S)" [F(1, 72) = 1.21, P = 0.26, ηp 2 = 0.02] was found. No significant interaction between "expectancy level" and "anxiety state (STAI-S)" [F(2, 72) = 1.68, P = 0.19, ηp 2 = 0.05] (see **Figure 4**, left panel), or between "anxiety state" and "gender" [F(2, 72) = 1.27, P = 0.26, ηp 2 = 0.02] was observed. However, the interaction between "expectancy level" and "gender" was significant [F(2, 72) = 4.04, P = 0.02, ηp 2 = 0.11]. Post-hoc comparison on this interaction revealed the same pattern as the results reported in the previous section ("Influence of expectancy level, dispositional optimism, and gender on placebo effects").

With regard to the reduction of unpleasantness, no main effect of "expectancy level" [F(2,72) = 0.12, P = 0.891, ηp 2 = 0.003], "anxiety state (STAI-S)" [F(1, 72) = 0.07, P = 0.796, ηp 2 = 0.001], or "gender" [F(1, 72) = 1.28, P = 0.263, ηp 2 = 0.018] was observed. The interaction between "expectancy level" and "anxiety state (STAI-S)" [F(2, 72) = 4.05, P = 0.022, ηp 2 = 0.106] (**Figure 4**, right panel), and the interaction between "expectancy level" and "gender" [F(2, 72) = 4.49, P = 0.015, ηp 2 = 0.117] (**Figure 2**,

right panel) were significant. Post-hoc pairwise comparisons on the interaction between "expectancy level" and "anxiety state (STAI-S)" showed that for participants with low STAI-S scores, those in High expectancy group felt less pain unpleasantness due to the placebo treatment than those in No expectancy group (P = 0.027). Post-hoc comparison on interaction between "expectancy level" and "gender" revealed the same pattern as the results reported in the previous section ("Influence of expectancy level, dispositional optimism, and gender on placebo effects"). No significant interaction was observed between "anxiety state (STAI-S)" and "gender" [F(2, 72) = 2.39, P = 0.127, ηp 2 = 0.034].

### DISCUSSION

In the present study, we demonstrated that placebo effects were not only influenced by expectancy level or personal characteristics alone, but also depended on their interactions. Specifically, we observed that the reductions of pain intensity and pain unpleasantness in the Test phase were influenced by the interaction between expectancy level and gender, as mainly reflected by greater reductions of pain intensity and pain unpleasantness in females at Low expectancy level than females at No/High expectancy levels, and greater reductions of pain intensity and pain unpleasantness in males than in females at High expectancy level. Additionally, the reduction of pain unpleasantness was modulated by the interaction between expectancy level and dispositional optimism, as well as the interaction between expectancy level and anxiety state. Participants who were more optimistic in Low expectancy group, or those who were less anxious in High expectancy group showed greater reductions of pain unpleasantness.

Firstly, placebo effects, defined as the reduction of pain intensity or unpleasantness, depended on the interaction between expectancy level and gender. We found female participants elicited maximal placebo effects in Low rather than No and High expectancy groups, which is in line with the previous

Inventory (Low STAI-S and High STAI-S) are marked in blue and red, respectively.

study showing that placebo effects, as quantified by systolic blood pressure, alertness, and tension, were stronger at the moderate expectancy level than at the extremely low and high expectancy levels (24). In other words, a realistically reasonable expectancy, rather than the unrealistic expectancy level, is more likely to enhance individual belief of the treatment, which is essential to maximize placebo effects (21, 24, 51). However, when compared with female participants, males exhibited a different pattern: in High expectancy group, they reported a greater reduction of pain intensity/unpleasantness due to placebo treatment. These findings suggested that a placebo response to an expectancy manipulation can vary tremendously by gender. However, we failed to observe the main effect of gender in placebo responses, which is inconsistent with a few previous studies (33, 34, 52). Admittedly, the issue of gender discrepancy in placebo responses is still controversial, and further investigation on this issue is highly needed. Please note that gender-specific placebo effects would have tremendous implications for medical research and clinical conditions, such as pain and neurological disorders, in which placebo responses are commonly considered relevant (53, 54).

Secondly, we provided evidence showing that placebo effects, defined as the reduction of pain unpleasantness, were influenced by the interaction between expectancy level and other personal characteristics, such as dispositional optimism and anxiety state. Previous evidence proved that individuals with high scores of dispositional optimism or low scores of anxiety state were more likely to respond to placebo treatment (36, 37). This is in line with our results demonstrating that optimists (those with high LOT-R scores) or participants with low STAI-S scores showed greater placebo responses after treatments. Obviously, being more optimistic or less anxious has a positive influence on the experience to a placebo treatment, as these individuals have a tendency to hold positive expectation (55). In particular, the present results might help explain the consistent correlation between dispositional optimism and positive medical outcomes (56–58). It is suggested that the different respondence between optimists and pessimists (those with low LOT-R scores) to placebo-related expectations may contribute to placebo response discrepancy. Noted that such an effect of dispositional optimism on placebo effects was confirmed in our study, but only observed in Low expectancy group, suggesting that a realistically reasonable, but not an overly-positive expectancy could optimize the influence of dispositional optimism on the placebo response. In other words, since optimists cannot be frequently driven by negative expectancy as forcefully as pessimists can, they might experience fewer negative events. Further, may it be the optimists, not the pessimists, who could be most likely to respond to a placebo-related expectancy for positive outcomes. The above speculation is consistent with a study on persuasion, in which optimists were more likely than pessimists to be persuaded by positively structural arguments (59). Therefore, an individual with high dispositional optimism might not only be less susceptible to negative expectancy, but also be more possible than those with lower dispositional optimism to benefit from positive expectancy, particularly at realistically optimized expectancy level. This is also prompted that patients with high dispositional optimism should be informed more frequently about a certain treatment with realistically positive expectancy to strengthen their responses in medical care. Future studies are needed to explore this issue under clinical conditions.

Importantly, in line with previous studies demonstrating that people's belief can be influenced by personal characteristics, such as optimism, neuroticism, and extraversion (25, 26, 60), our observation provides further evidence suggesting that the placebo effect can be jointly affected by the expectancy level and personal characteristics, which is fitted well with the Response Expectancy Theory (24, 51). Notably, there are tremendous differences in personal characteristics between healthy population and patients. For example, depressive, persistent social phobic, neurotic, fearful, and obsessive-compulsive personality characteristics are very common in pain sufferers compared to healthy population, whereas patients undergoing injectable aesthetic treatments scored significantly higher on extraversion, agreeableness, openness to experience, and neuroticism (61–63). Thus, the next important step is to replicate the main findings of the present study in clinical conditions. To note, a growing body of neurobiological researches on placebo effects indicated the influence of cognitive progressing on the modulation of pain perception (64, 65), which implied that an integrated model combining cognitive factors with psychological factors is warranted to comprehensively explore the placebo mechanisms.

#### LIMITATIONS

There are two limitations in the present study. First, although we assigned both male and female experimenters randomly to the participants, we did not control the potential influence of experimenters' gender well-enough, which still could have increased error variance. Selecting either a male or a female experimenter might be more suitable for further investigations. Second, we examined the effect of the interaction between expectancy level and personal characteristics on placebo effects within a non-clinical population, and it calls for clinical studies to replicate the main findings of the present study.

#### CONCLUSION

Considering that placebo effects have been recognized as effective psychobiological events attributing to the improvement of the overall therapeutic outcomes, we believe that our findings not only advance our understanding of the psychological underpinnings of placebo effects, but also suggest a constructive way (regulating the expectation level individually based on the

#### REFERENCES

assessment of personal characteristics) to maximize placebo effects in various clinical applications.

### ETHICS STATEMENT

This experiment was approved by the Ethics Committee of Southwest University, China, and registered with ChiCTR1800014737 through Chinese Clinical Trial Register Centre. All procedure was carried out in accordance with the relevant approved lines.

### AUTHOR CONTRIBUTIONS

HW, LW, XJL, and LH conceived and designed the experiments. HW and HZ performed the experiments. LZ, XJL, and LH analyzed the data. LZ, HW, XYL, CB, LW, XJL, and LH wrote the paper. All authors approved the final manuscript and agreed to be accountable for all aspects of the work.

#### FUNDING

This work was supported by the National Natural Science Foundation of China (No. 31671141, 31701000, 31822025), the Informatization Special Project of Chinese Academy of Sciences (No. XXH13506-306), and the Scientific Foundation project of Institute of Psychology, Chinese Academy of Sciences (No. Y6CX281007, Y6CX021008, KLMH2018ZG02). The funders had no role in study design, data collection, data analysis, decision to publish, or preparation of the manuscript.

65. Zhang H, Zhou L, Wei H, Lu X, Hu L. The sustained influence of prior experience induced by social observation on placebo and nocebo responses. J Pain Res. (2017) 10:2769. doi: 10.2147/JPR.S1 47970

**Conflict of Interest Statement:** The authors declare that the research was conducted in the absence of any commercial or financial relationships that could be construed as a potential conflict of interest.

Copyright © 2019 Zhou, Wei, Zhang, Li, Bo, Wan, Lu and Hu. This is an open-access article distributed under the terms of the Creative Commons Attribution License (CC BY). The use, distribution or reproduction in other forums is permitted, provided the original author(s) and the copyright owner(s) are credited and that the original publication in this journal is cited, in accordance with accepted academic practice. No use, distribution or reproduction is permitted which does not comply with these terms.

# Influencing Side-Effects to Medicinal Treatments: A Systematic Review of Brief Psychological Interventions

Rebecca K. Webster 1,2 \* and G. James Rubin1,2

*1 Department of Psychological Medicine, Institute of Psychiatry, Psychology & Neuroscience, King's College London, London, United Kingdom, 2 The National Institute for Health Research Health Protection Research Unit in Emergency Preparedness and Response, King's College London, London, United Kingdom*

Background: Nocebo effects contribute to a large proportion of the non-specific side-effects attributed to medications and are mainly generated through negative expectations. Previous reviews show that interventions designed to change participants' expectations have a small effect on pain experience. They are also effective in reducing side-effects caused by exposure to sham medications. To date, there has been no review of the influence of such interventions on symptoms attributed to real medicinal treatments.

#### Edited by:

*Luana Colloca, University of Maryland, Baltimore, United States*

#### Reviewed by:

*Meike C. Shedden-Mora, University Medical Center Hamburg-Eppendorf, Germany Karin Meissner, Ludwig Maximilian University of Munich, Germany*

> \*Correspondence: *Rebecca K. Webster<EMAIL_ADDRESS>
#### Specialty section:

*This article was submitted to Psychosomatic Medicine, a section of the journal Frontiers in Psychiatry*

Received: *24 October 2018* Accepted: *24 December 2018* Published: *05 February 2019*

#### Citation:

*Webster RK and Rubin GJ (2019) Influencing Side-Effects to Medicinal Treatments: A Systematic Review of Brief Psychological Interventions. Front. Psychiatry 9:775. doi: 10.3389/fpsyt.2018.00775* Objective: To review studies using a randomized controlled design testing the effect of brief psychological interventions compared to usual practice on the side-effect experience to medicinal treatments in healthy volunteers and patients.

Methods: We searched Web of Science, Scopus, Medline, PsycINFO, PsycARTICLES, and Cochrane CENTRAL using search terms for randomized controlled trials along with "nocebo," "placebo effect," "medication," "side-effects," and associated terms. Studies were eligible if they studied a human population, used an active medicine, delivered a brief psychological intervention intended to influence side-effect reporting compared to usual care or no intervention, and used a randomized controlled design. Because of the heterogeneity of the literature we used a narrative synthesis and assessed evidence quality using the GRADE approach.

Results: Our database search and supplementary search of the reference sections of included studies retrieved 50,140 citations. After screening, full text review and manual reference searches, 27 studies were included. The quality of the studies and evidence was judged to be low. The strongest and most consistent effect came from omitting side-effect information, although surprisingly de-emphasizing side-effects did not affect side-effect reporting. Other techniques, including priming, distraction, and altering the perception of branding, produced mixed results.

Conclusion: Brief psychological interventions can influence side-effect reporting to active medications. Research is currently investigating new ways to de-emphasize side-effects whilst still upholding informed consent, but larger confirmatory trials with suitable control groups are needed. The literature in this area would be improved by more detailed reporting of studies.

Keywords: review, side-effects, medicine, nocebo effect, interventions, side-effect information

## INTRODUCTION

Nocebo effects, sometimes dubbed the placebo effect's "evil twin," are the experience of noxious symptoms in response to an inert exposure (1). Nocebo effects can also refer to negative clinical outcomes which are not attributable to the actual pharmacological or physiotherapeutic action of an intervention (2). It is estimated that between 38 and 100% of side-effects reported to drugs taken for a large range of medical conditions are related to the treatment context, rather than the active ingredients of the medication itself (3).

These nocebo-related side-effects are important, as they can affect a patient's well-being (4) and influence their decision as to whether to adhere to their treatment regimen (5, 6). For example adverse media coverage surrounding the safety of statins and their reported side-effects has resulted in around 2,00,000 patients who are no longer taking their statins as directed leading to a predicted increase of 2,000 cardiovascular events in the next decade (7). This is despite the fact that most of these side-effects are probably nocebo-related (8). Perhaps unsurprisingly, sideeffects can also result in substantial additional health care costs in terms of additional primary care and hospital visits and also the cost of wasted medication due to non-adherence (9).

Of the multiple factors that may contribute to the development of nocebo effects, expectations of symptoms appear to be the main contributor. These can be generated through verbal and written suggestions about what symptoms to expect, be implied by the apparent dose of a drug, and be learnt through classical conditioning and social observation (10). Studies have used these psychological mechanisms as a means to alter peoples' experience of experimentally induced pain (11), as well as pain following acute medical procedures, such as injections (12) and surgery (13). These effects have been studied in multiple reviews, showing that brief psychological interventions designed to change expectation of pain following treatment have a small but reliable effect on relieving patients' pain compared to usual care (14–16).

However, to our knowledge, there has been no review of whether such interventions can alter patient experience ofsideeffects to medicinal treatments. Although evidence demonstrates that such interventions can be effective in altering side-effects reported following exposure to inert substances (10), it is also important to assess if these effects can be transferred to clinical practice. We therefore set out to review studies using a randomized controlled design testing the effect of brief psychological interventions compared to usual practice on the side-effect experience to medicinal treatments in healthy volunteers and patients. To answer the question: can brief psychological interventions influence the side-effect experience to medications?

### METHODS

Our reporting of this systematic review adheres to the standards for the Preferred Reporting Items for Systematic reviews and Meta-Analyses (17). The protocol for this review was prospectively registered on PROSPERO (CRD42018091903).

### Identification of Studies

We searched the following electronic databases with a predefined search strategy: Web of Science, Scopus, OvidSp (Medline, PsycINFO, and PsycARTICLES) and Cochrane CENTRAL. We included Web of Science and Scopus for their coverage of the sciences and social sciences. OvidSp was chosen for its coverage of journals chiefly in the area of health sciences, and also for its inclusion of the databases PsycINFO and PsycARTICLES. Cochrane CENTRAL was included due to its coverage of randomized controlled trials and because it includes records which are derived from other sources to the ones already chosen.

In preliminary work we tested a variety of search strategies in an effort to balance specificity and sensitivity. Our final search strategy used the recommended search terms to identify randomized controlled trials (18) along with the terms and associated words for "nocebo," "placebo effect," "medication," and "side-effects." We used separate search strategies for each of the databases as these needed to be modified due to differences in MeSH terms, boolean operators and wildcards. A copy the search strategy we used for Medline can be seen in the **Supplementary Material**.

### Review Process

The search was initially carried out on 22nd March 2018 and updated on 22nd June 2018 following the identification of a relevant study published between this time. The initial electronic searches were combined using EndNote and duplicates were identified and deleted. The titles and abstracts of citations were then screened for potential relevance. If relevance was not clear from the abstract, the study was taken forward to the full text review. All full text versions of papers that were potentially relevant were then screened in relation to the inclusion criteria. Papers that met the inclusion criteria had their reference sections manually searched for other studies that could be included.

### Selection Criteria

Studies were eligible for inclusion in this review if they met the criteria below.

#### Population

Human population (healthy volunteers, patients and children were allowed).

#### Exposure

Active medicinal treatment (i.e., contains a pharmacological agent), associated with side-effects.

#### Intervention

A brief, psychological intervention delivered in one session and that could be feasibly introduced within a single doctorpatient consultation or treatment appointment. By psychological we mean an intervention that targets certain psychological processes, such as cognitive expectations, attention or learning. Interventions requiring biological or chemical stimuli were excluded because these are not purely psychological. As we wanted to identify interventions that could be easily incorporated into clinical practice, in-depth psychological interventions, such as cognitive behavior therapy, mindfulness, relaxation training or guided imagery, or that consisted of intensive educational packages were excluded as these typically are not delivered in one session and often take place over the course of a treatment.

#### Comparator

Usual care. We excluded studies with control conditions involving a different type of intervention.

#### Outcome

We included studies with an outcome of side-effects measured via self-report or inferred through objective measures. We followed the NICE (19) definition of a side-effect as "An effect of a drug (or treatment or intervention) that is additional to the main intended effect. It could be good, bad or neutral, depending on the circumstances." For some studies, e.g., those concerning infant experience to vaccinations, side-effects were measured within minutes of the procedure. We excluded these on the bases that the "side-effects" were presumably related to the insertion of the needle rather than the effects of the vaccine itself.

#### Study Design

Used an experimental design in which participants were randomized or quasi randomized to receive the intervention or the control condition.

#### Other Criteria

Published in the English language.

#### Data Extraction

We extracted data from the final set of studies using a data extraction table developed for this systematic review. Data extracted included the study design and methodology, main demographics of participants, description of intervention and control conditions, side-effect measures, statistical approach and results. We also extracted details about the mode of the intervention, its content and duration.

### Quality Assessment

We assessed the quality of all eligible studies using the Cochrane Collaboration's Risk of Bias tool for randomized controlled trials (20).

### Data Synthesis and Analysis

Due to the heterogeneity in the interventions that we included and the way that side-effects were measured, scored and analyzed, we used a narrative synthesis to analyse the results. There is no general consensus on the best way to carry out a narrative synthesis for systematic reviews (21). As such we decided to use a weight of evidence approach by identifying the quality of evidence for each type of intervention reviewed. To do this we used the GRADE approach (22) which is a transparent framework used to grade the quality of evidence included in systematic reviews and the strength of recommendations.

### RESULTS

#### Search Results

The database search retrieved 50,133 citations and searching the reference lists of included studies retrieved another 7, giving a total of 50,140. After removing duplicates 40,346 citations remained. After screening titles and abstracts, we reviewed the full text of 63 articles relating to 66 studies. Of these, 39 studies were excluded for not meeting the inclusion criteria, resulting in a total of 26 articles reporting on 27 studies. One article (23) reported results on two separate studies and is referred to in the text and tables as Study 1 or Study 2 where necessary. The number of studies at each stage of the search strategy and the reasons for exclusion are shown in **Figure 1**.

### Study Characteristics

See **Table 1** for a full summary of the characteristics of the included studies. The 27 studies included in the review reported on a total of 3,459 participants. There was a range of patient groups and treatments under investigation. The most common of these were patients with cancer receiving chemotherapy (26, 31, 39, 41–44, 46), and patients with depression prescribed anti-depressants (29, 32, 35–37). All studies used a between participants RCT design apart from Cildag et al. (24), Myers and Calvert (36), Redd et al. (39), and Schagen et al. (42) which used a quasi-randomized approach, and Faasse et al. (28) who used a within-subjects RCT design. Some studies used a factorial design in their RCT involving different experimental conditions or baseline variables entered as independent factors (23, 31, 39, 41–43). In these cases, we have reported the main effects of the relevant intervention under investigation.

There were a variety of interventions used by included studies. We looked for common themes and content of the various interventions and were able to group the studies into five different types, these were: priming, distraction, branding, omitting sideeffects, and de-emphasizing side-effects, plus a miscellaneous group.

The majority of studies used an un-validated questionnaire specifically designed for their study to measure side-effects, and measures were generally completed within days/weeks following treatment initiation.

### Quality Assessment

The quality of included studies was poor (see **Figures 2**, **3**). The main problem was a lack of clear reporting within the papers. Over half of the studies neglected to mention how they carried out randomization, and four were at high risk for using a quasi-randomized approach. Because of the unclear reporting of random sequence generation, the risk for allocation concealment bias followed a similar pattern, and six studies were at high risk because their randomization approach allowed research staff to foresee subsequent allocations. For blinding of participants and personnel, studies often failed to state whether the experimenters were blind to the manipulation that accompanied the active treatment, leaving the risk of bias unclear. Only seven studies used adequate blinding procedures, with one not using blinding at all. Nineteen studies used side-effect measures which were completed by participants, as such blinding of the outcome assessment was judged unlikely to influence these results. For the remaining eight studies it was unclear if participants filled in the measures themselves or if they were administered by a blind/non-blind member of the study team. For 16 studies, drop outs were not addressed, or if they were, the paper typically failed

FIGURE 1 | Flow diagram of the selection process of studies including the number of events and reasons for exclusion.

to explain how this affected the results, leaving the risk of bias unclear; the remaining 11 studies provided adequate information and reasoning behind drop outs. Only two studies had lodged a protocol in a publicly accessible registry before the start of recruitment, leaving us unable to assess the risk for selective reporting for the remaining studies, apart from one in which there was a change in the prespecified primary analysis suggesting there was a high risk of bias.

#### Quality of the Evidence

The quality of evidence regarding priming, distraction, omitting side-effect information and de-emphasizing side effects, and doctor characteristic intervention(s) was very low. This is because most of the information came from studies at low or unclear risk of bias, in which plausible bias could alter the results. There was also some evidence of inconsistency and imprecision in the results due to opposite findings, wide confidence intervals and some small studies which may not have been adequately powered. Due to the broad nature of this systematic review, there is no evidence of indirectness, as all included studies helped to answer the question. It is plausible however, there may have been some publication bias due to the preponderance of smaller studies.

The quality of evidence regarding the branding intervention studies was low. This was graded similarly due to the reasons discussed for the above interventions, however the inconsistency in the results could perhaps be explained by differences in the interventions, and we judged that the small studies were probably due to this literature representing an early evidence base, rather than publication bias.

Finally, the quality of evidence for the deception intervention was moderate. There was some imprecision evident and the sample size was small, however the study was judged to have a low overall risk of bias, and there was no evidence of indirectness. As only one study was included, inconsistency and publication bias could not be determined.

#### Effect of Interventions on Side-Effect Reporting Priming

#### Four studies looked at the effect of priming on side-effect reporting following chemotherapy with mixed results (see

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**Table 2**). Colagiuri et al. (26) found a slight trend for priming patients by assessing their expectancies for side-effects vs. no assessment on subsequent nausea. Jacobs et al. (31) and Schagen et al. (42) found no indication of an effect of priming patients by mentioning that chemotherapy is associated with cognitive problems on retrospectively reported cognitive sideeffects. However, Schagen et al. (43) in a similar study did find a small effect of priming leading to increased reporting of previous cognitive side-effects to chemotherapy compared to those in a control group who received no such information.

#### Distraction

Three studies looked at the effect of distraction on side-effect reporting following chemotherapy and drug provocation tests, showing some evidence that distraction can reduce side-effect reporting (see **Table 3**). Cildag et al. (24) found that keeping patients busy with filling/archiving files significantly reduced the occurrence of adverse reactions compared to a control group, but only by a small amount. Redd et al. (39) found that distracting pediatric cancer patients with video games significantly reduced chemotherapy nausea from baseline, compared to those in the control group. However, for adult cancer patients, Vasterling et al. (46) found that video games were not effective in reducing chemotherapy nausea or vomiting compared to a control group.

#### Branding

Two studies looked at the effect of branding on side-effect reporting to ibuprofen showing some evidence that branding can affect side-effect reporting (see **Table 4**). Colgan et al. (27) found that a video designed to correct participants' beliefs about generic medicines significantly reduced side effects for both branded and generic ibuprofen compared to those in a control group, showing a large effect. However, Faasse et al. (28) found that simply changing the labeling of ibuprofen from branded to generic did not significantly affect side-effect reporting.

#### Omitting Side-Effect Information

Eleven studies looked at the effect of omitting side-effect information on side-effect reporting to a range of different treatments, showing that omitting side-effects significantly decreases side-effect reporting (see **Table 5**). Eight studies

#### TABLE 2 | Priming intervention results.

*Ns, non-significant; M, mean; SE, standard error; SD, standard deviation; OR, odds ratio; d, Cohen's d; –, insufficient detail to calculate effect size.*

#### TABLE 3 | Distraction intervention results.

*Ns, non-significant; M, mean; OR, odds ratio; –, insufficient detail to calculate effect size.*

found that not informing patients about potential side-effects significantly decreased side-effect reporting to metropolol (25), a myelogram (30), antidepressants (32), finasteride (34), skin cream (23) (study 1 and 2), atenolol (45), and montekulast (48) compared to a control group which received side-effect information, each showing large effect sizes. Similarly Myers and Calvert (36) found a trend for a decrease in side-effect reporting when patients were not informed about the sideeffects to the antidepressant dothiepin compared to a control group, and Myers and Calvert (37) found that side-effects significantly decreased to dothiepin when comparing the group that only received beneficial information to groups that received no information and side-effect information. Only one study, Myers and Calvert (35), found no effect of side-effect information on subsequent side-effect reporting.

#### De-emphasizing Side-Effects

Five studies looked at the effect of de-emphasisng side-effects on side-effect reporting to range of different treatments, showing evidence that this seems to have no effect (see **Table 6**). Three studies found that informing patients of side-effects but in a way that does not make them seem as bad had no effect on sideeffect reporting to anesthesia (33), or chemotherapy (41, 44), however this was compared to a control group that did not receive any information about side-effects. O'Connor et al. (38) found that positively framing side-effects to emphasize those that remain side-effect free and comparing to a control group that received standard information about side-effects significantly reduced side-effect reporting to the flu vaccine. Wilhelm et al. (47) found that positively framing side-effects by explaining they are a sign that the drug is working did not significantly reduce side-effects to metoprolol compared to those who received standard information.

#### Other Interventions

Two other studies investigated interventions which do not fall into the above categories (see **Table 7**). Faria et al. (29) deceptively told seasonal affective disorder patients that they would receive an active placebo which would produce similar side-effects to escitalopram when in fact they received the active drug itself

TABLE 4 | Branding intervention results.

*Ns, non-significant; M, mean; SE, standard error; d, Cohen's d; –, insufficient detail to calculate effect size.*