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• W2065994042 abstract "This article summarizes recent progress and regulatory guidance on design of trials to assess the efficacy of new therapies for functional gastrointestinal disorders (FGIDs). The double-masked, placebo-controlled, parallel-group design remains the accepted standard for evaluating treatment efficacy. A control group is essential, and a detailed description of the randomization process and concealed allocation method must be included in the study report. The control will most often be placebo, but for therapeutic procedures and for behavioral treatment trials, respectively, a sham procedure and control intervention with similar expectation of benefit, but lacking the treatment principle, are recommended. Investigators should be aware of, and attempt to minimize, expectancy effects (placebo, nocebo, precebo). The primary analysis should be based on the proportion of patients in each treatment arm who satisfy a treatment responder definition or a prespecified clinically meaningful change in a patient-reported outcome measure. Data analysis should use the intention-to-treat principle. Reporting of results should follow the Consolidated Standards for Reporting Trials guidelines and include secondary outcome measures to support or explain the primary outcome and an analysis of harms data. Trials should be registered in a public location before initiation and results should be published regardless of outcome. This article summarizes recent progress and regulatory guidance on design of trials to assess the efficacy of new therapies for functional gastrointestinal disorders (FGIDs). The double-masked, placebo-controlled, parallel-group design remains the accepted standard for evaluating treatment efficacy. A control group is essential, and a detailed description of the randomization process and concealed allocation method must be included in the study report. The control will most often be placebo, but for therapeutic procedures and for behavioral treatment trials, respectively, a sham procedure and control intervention with similar expectation of benefit, but lacking the treatment principle, are recommended. Investigators should be aware of, and attempt to minimize, expectancy effects (placebo, nocebo, precebo). The primary analysis should be based on the proportion of patients in each treatment arm who satisfy a treatment responder definition or a prespecified clinically meaningful change in a patient-reported outcome measure. Data analysis should use the intention-to-treat principle. Reporting of results should follow the Consolidated Standards for Reporting Trials guidelines and include secondary outcome measures to support or explain the primary outcome and an analysis of harms data. Trials should be registered in a public location before initiation and results should be published regardless of outcome. Clinical trial design for functional gastrointestinal disorders (FGIDs) is hampered by several factors, including symptom variability between subjects or groups and within subjects over time and the lack of specific biomarkers. The Rome diagnostic criteria and design recommendations are now routinely applied in clinical treatment trials. Since the publication of the Rome III guidance, there have been substantial advances in several aspects of clinical trial design. The expectations for patient-reported outcome (PRO) measurement have undergone major changes with the dissemination of regulatory guidelines for PROs from the US Food and Drug Administration (FDA) and the European Medicines Agency (EMA).1Corsetti M. Tack J. FDA and EMA end points: which outcome end points should we use in clinical trials in patients with irritable bowel syndrome?.Neurogastroenterol Motil. 2013; 25: 453-457Crossref PubMed Scopus (37) Google Scholar, 2US Department of Health and Human Services, Food and Drug Administration, Center for Drug Evaluation and Research (CDER). Guidance for Industry: Irritable Bowel Syndrome−Clinical Evaluation of Drugs for Treatment. Available at: http://www.fda.gov/downloads/Drugs/Guidances/UCM205269.pdf. Published May 2012. Accessed January 10, 2015.Google Scholar, 3European Medicines AgencyGuideline on the Evaluation of Medicinal Products for the Treatment of Irritable Bowel Syndrome. Vol 2014. EMA, London, UK2013Google Scholar Accumulating data also provide new insights for measuring common FGID symptoms, such as abdominal pain, discomfort, diarrhea, urgency, constipation, and bloating, among others. New information about the placebo, “nocebo,” and “precebo” responses also challenges researchers to consider the biases inherent in FGID trials. In addition, advances in pragmatic clinical trial (PCT) design offer new approaches to measuring the effectiveness of FGID therapies in the context of everyday clinical practice. This updated Rome IV chapter now addresses each of these new trends, provides guidance for investigators seeking to develop and conduct FGID clinical trials, and emphasizes evolving concepts about how best to test the risks and benefits among the full range of FGID treatments. The first task is to establish the hypothesis of the putative effect of the studied treatment, based on its expected mechanism of action, which generates the specific research question(s) for the proposed trial. As multiple factors contribute to the pathogenesis of FGIDs, it is likely that no single therapeutic approach will fully abolish all symptoms. Most FGID intervention studies evaluate the impact of a treatment on the items listed in Table 1, but specific goals can vary widely. Investigators should prioritize their research question(s) pertinent to the specific FGID, develop a hypothesis based on available evidence, and design a study that most effectively answers the research question(s).Table 1Goals of a Treatment TrialTo ascertain the ability of the intervention to Relieve symptoms or decrease symptom severity Improve functional health status and health-related quality of life Improve ability to cope with symptoms Decrease use of health care resources Avoid harm and be cost-effective Open table in a new tab In general, the primary question will address whether the study treatment improves FGID symptoms. Consequently, the primary outcome measurement tools must include reporting of the most important symptoms expected to change with the proposed treatment. The secondary questions are best determined by the particular disorder, that is, its specific symptoms and the mechanism of action of the treatment. Pathophysiological factors, while important explanatory parameters, should be considered secondary rather than primary end points. A screening log of key variables is mandatory in order for readers to judge the generalizability of the results. The log should include demographic (eg, age, sex, and race) and clinical variables (eg, disease severity, symptom duration, prior treatments for the condition, and the use of concurrent medications) for patients entered and excluded, with reasons for exclusion. Explicit inclusion and exclusion criteria are mandatory for all studies. Most treatment trials in FGIDs have required a minimum severity level for specific symptoms thought to be typical of the condition. Balanced consideration for the potential mechanism of action of the drug must also be given when selecting the study population. It is advisable to include as broad a spectrum of patients as possible, defined by the Rome- specific FGID criteria. Restricting or modifying the study population must be justified. The EMA requests that early drug development programs include sufficient numbers of both men and women to permit assessment of safety and efficacy for both sexes. The FDA also supports engagement of subjects of different racial backgrounds.2US Department of Health and Human Services, Food and Drug Administration, Center for Drug Evaluation and Research (CDER). Guidance for Industry: Irritable Bowel Syndrome−Clinical Evaluation of Drugs for Treatment. Available at: http://www.fda.gov/downloads/Drugs/Guidances/UCM205269.pdf. Published May 2012. Accessed January 10, 2015.Google Scholar, 3European Medicines AgencyGuideline on the Evaluation of Medicinal Products for the Treatment of Irritable Bowel Syndrome. Vol 2014. EMA, London, UK2013Google Scholar The minimum screening for eligibility should be specified and should adhere to current guidelines. The Rome classification of FGIDs is currently the most comprehensive and well-established diagnostic system, and its use ensures a sufficient degree of standardization of study participants across centers and cultural settings, and allows further exploration for differences in treatment response. Important confounding factors to consider for possible exclusion criteria are psychological comorbidities, sociocultural perspectives, and biological variations. Psychological comorbidities are often thought to be predictors of poor response to treatment, but this has not been proven.4Holtmann G. Kutscher S.U. Haag S. et al.Clinical presentation and personality factors are predictors of the response to treatment in patients with functional dyspepsia; a randomized, double-blind placebo-controlled crossover study.Dig Dis Sci. 2004; 49: 672-679Crossref PubMed Scopus (43) Google Scholar Other psychologically related influences include the placebo and nocebo effects (see section on placebo and nocebo), and future studies may wish to consider designs that could measure the subject’s proneness to these effects. Overlap disorders, potential disease modifiers, and important comorbidities that might affect treatment response should be assessed and explored. The overlap of FGIDs with other FGIDs and with somatic and psychiatric disorders is a challenge for clinical trail design. First, the accuracy of the FGID diagnosis may be questioned and it is possible that a treatment might improve the symptoms of one disorder while symptoms of the other worsen. Second, the presence of a comorbidity may be associated with increased symptom severity, greater impact on health-related quality of life (HRQOL), and greater psychological distress—all of which could modify the response to treatment. Third, underlying motility or sensory disorders in different parts of the GI tract may interact in ways that could affect the response to specific treatments. The committee recommends that, in most situations, patients with overlapping conditions be included in the trial and the presence of comorbid conditions should be documented. Continuing research is needed to identify biomarkers that attempt to elucidate disease mechanisms and may facilitate assessment of efficacy of treatments in FGID studies. A biomarker is an indicator of a physiological or pathological state that can be objectively measured and evaluated, in contrast to PROs, which are measured using questionnaires that capture patient perceptions of their illness.5Spiller R.C. Potential biomarkers.Gastroenterol Clin N Am. 2011; 40: 121-139Abstract Full Text Full Text PDF PubMed Scopus (22) Google Scholar A valid and reliable biomarker should optimally distinguish patients with a known clinical syndrome from other conditions, and do so with a high degree of sensitivity and specificity. It may also have predictive value, in that its presence could potentially predict natural history and/or response to specific therapies.5Spiller R.C. Potential biomarkers.Gastroenterol Clin N Am. 2011; 40: 121-139Abstract Full Text Full Text PDF PubMed Scopus (22) Google Scholar While they are not suitable as surrogate end points at this time, they can be used to stratify patients. However, at present, very few biomarkers have been identified that have sufficient sensitivity and specificity. There are several challenges to conducting FGID treatment trials, including a high placebo response rate6Spiller R.C. Problems and challenges in the design of irritable bowel syndrome clinical trials: experience from published trials.Am J Med. 1999; 107: 91S-97SAbstract Full Text Full Text PDF PubMed Scopus (149) Google Scholar; symptoms that are intermittent and of fluctuating severity7Palsson O.S. Baggish J. Whitehead W.E. Episodic nature of symptoms in irritable bowel syndrome.Am J Gastroenterol. 2014; 109: 1450-1460Crossref PubMed Scopus (30) Google Scholar; a potential need for multimodal therapy, given the limited efficacy of available treatments or multiple etiological mechanisms affecting the disease process8Drossman D.A. Thompson W.G. The irritable bowel syndrome: review and a graduated multicomponent treatment approach.Ann Intern Med. 1992; 116: 1009-1016Crossref PubMed Scopus (279) Google Scholar; difficulty maintaining masking of patients and investigators in trials of behavioral interventions9Whitehead W.E. Control groups appropriate for behavioral interventions.Gastroenterology. 2004; 126: S159-S163Abstract Full Text Full Text PDF Scopus (41) Google Scholar; contamination from over-the-counter treatments or medicines taken for other conditions; the necessity of avoiding significant harms10Camilleri M. Safety concerns about alosetron.Arch Intern Med. 2002; 162: 100-101Crossref PubMed Google Scholar in treating non−life-threatening conditions; absence of biomarkers both for diagnosing the disorder in question and for evaluating the treatment response; and absence of acceptable end points for many FGIDs. In addition, clinical trials differ from clinical practice in several ways, including the application of strict inclusion and exclusion criteria, the use of a placebo group, application of a standardized intervention, frequent follow-up visits with extensive data recording, and the use of study coordinators. The placebo response observed in clinical trials has been attributed in part to the attention given to enrolled subjects, including detailed explanation and reassurance, close monitoring, and ready access to study coordinators, which may in themselves produce a therapeutic effect. Bias, defined as “systematic error” in estimating the treatment effect, may enter a clinical trial at any stage, from design to publication.11Sackett D.L. Bias in analytic research.J Chronic Dis. 1979; 32: 51-63Abstract Full Text PDF PubMed Scopus (1653) Google Scholar The major sources of bias are listed in Table 2.Table 2Major Sources of Bias in Clinical TrialsBias typeCommentsInvestigator biasConscious or unconscious, usually expressed through decisions about eligibilityPatient expectancy (placebo)Especially a problem where end points are subjectiveAscertainment bias Self-selection for treatmentPatients are more likely to respond positively to treatments they prefer and seek out Changes in subject poolPublicity or other factors may influence the subject pool over timeNonspecific effects Doctor−patient relationshipEspecially important in psychological interventions Regression to the meanPatients are usually enrolled when most symptomatic and inevitably improvePublication biasAuthors are more likely to submit trials with positive results and journals are more likely to publish them Open table in a new tab It is mandatory to undertake the maximum masking possible, determined by the type of intervention and study design. It is recommended to evaluate and report whether masking was successful. Masking of participants, investigators, and evaluators to treatment assignment is a key feature of a successful controlled trial.12Jamshidian F. Hubbard A.E. Jewell N.P. Accounting for perception, placebo and unmasking effects in estimating treatment effects in randomised clinical trials.Stat Methods Med Res. 2011; 23: 293-307Crossref Scopus (13) Google Scholar Single masking is when only the study subject/patient is unaware of the treatment allocation. Double-masking (both patients and research personnel) is necessary to ensure the highest validity of the primary outcome measurement. Triple-masking includes also masking monitors, data managers, statisticians, and others who interpret outcome tests.13Spilker B. External influences on protocol design.Epilepsy Res Suppl. 1993; 10: 115-124Google Scholar Interventions involving procedures such as psychotherapy, hypnotherapy, sphincterotomy, or drug trials in which the active drug causes predictable side effects or rapid symptom changes, are difficult to mask from patients or investigators. Possible solutions include using independent assessors who are unaware of the intervention, or standardized interviewer-administered or self-administered questionnaires.14Devilly G.J. Borkovec T.D. Psychometric properties of the credibility/expectancy questionnaire.J Behav Ther Exp Psychiatry. 2000; 31: 73-86Crossref PubMed Scopus (1298) Google Scholar In addition, study investigators are encouraged to ask both patient and interventionist at the end of the trial whether they believe active treatment was administered and to report these data. Investigators must include a detailed description of their randomization process and concealed allocation method in the report of the study. Randomization is the process of assigning subjects to different treatment arms without bias, which can be accomplished either by someone other than an investigator preparing a numbered series of sealed envelopes containing group assignments or use of a computer program for random allocation.13Spilker B. External influences on protocol design.Epilepsy Res Suppl. 1993; 10: 115-124Google Scholar, 15Altman D.G. Randomisation.BMJ. 1991; 302: 1481-1482Crossref PubMed Scopus (141) Google Scholar Critical recommendations to ensure randomized concealed treatment are the randomization code is generated by a noninvestigator (preferably a computer), randomization is done within blocks of variable size (permuted block randomization) or sufficient size to minimize unmasking due to side effects in previously exposed patients, the list of patient treatment assignments should be available only to the medical officer in charge of patient safety, and a record should be kept of patients for whom the mask has been broken. When reporting the trial, the randomization procedure should be described explicitly.15Altman D.G. Randomisation.BMJ. 1991; 302: 1481-1482Crossref PubMed Scopus (141) Google Scholar Stratified randomization is a variation on randomization that is designed to assure balance on the most important prognostic factors by using a separate randomization sequence for each stratum (eg, male vs female or IBS with constipation [IBS-C] vs IBS with diarrhea ]IBS-D])16Altman D.G. Comparability of randomised groups.Statistician. 1985; : 125-136Crossref Google Scholar. A control group is required to establish the true efficacy of a new treatment. As therapies of proven efficacy accumulate, a comparison against an active available treatment can be considered, but this requires higher patient numbers to establish efficacy and may fail to show a statistically significant difference.17Tinmouth J.M. Steele L.S. Tomlinson G. et al.Are claims of equivalency in digestive diseases trials supported by the evidence?.Gastroenterology. 2004; 126: 1700-1710Abstract Full Text Full Text PDF PubMed Scopus (26) Google Scholar, 18Temple R.J. When are clinical trials of a given agent vs. placebo no longer appropriate or feasible?.Control Clin Trials. 1997; 18 (discussion 661−666): 613-620Abstract Full Text PDF PubMed Scopus (50) Google Scholar Control groups for therapeutic procedures are equally crucial. In behavioral treatment trials, confirming that the control intervention produces a similar expectation of benefit but does not act on the same physiological or psychological principle is recommended. In trials involving a therapeutic procedure, a sham group is recommended when feasible. Placebo (from the Latin “to please”) is an intervention that generates the expectation of benefit in the patient but is believed to lack any specific effect to change a particular disorder,19Thompson W.G. Placebos: a review of the placebo response.Am J Gastroenterol. 2000; 95: 1637-1643Crossref PubMed Google Scholar or an intervention for which there is no scientific theory explaining its action.20Bernstein C.N. Placebos in medicine.Semin Gastrointest Dis. 1999; 10: 3-7PubMed Google Scholar When used along with blinding, use of a placebo design may enable investigators to assess side effects of interventions more readily and with less bias. Placebos can be administered as a drug or as a procedural intervention.20Bernstein C.N. Placebos in medicine.Semin Gastrointest Dis. 1999; 10: 3-7PubMed Google Scholar The placebo effect is well characterized in FGID trials, especially in FD and IBS, with response rates ranging from 6%−72%21Veldhuyzen van Zanten S.J. Cleary C. Talley N.J. et al.Drug treatment of functional dyspepsia: a systematic analysis of trial methodology with recommendations for design of future trials.Am J Gastroenterol. 1996; 91: 660-673PubMed Google Scholar, 22Musial F. Klosterhalfen S. Enck P. Placebo responses in patients with gastrointestinal disorders.World J Gastroenterol. 2007; 13: 3425-3429Crossref PubMed Scopus (56) Google Scholar and 0%−84%, respectively.6Spiller R.C. Problems and challenges in the design of irritable bowel syndrome clinical trials: experience from published trials.Am J Med. 1999; 107: 91S-97SAbstract Full Text Full Text PDF PubMed Scopus (149) Google Scholar A meta-analysis suggested that the placebo response is larger when a responder is defined by a global improvement in IBS symptoms compared with defining a responder by reduction in abdominal pain.23Vase L. Robinson M.E. Verne G.N. et al.The contributions of suggestion, desire, and expectation to placebo effects in irritable bowel syndrome patients. An empirical investigation.Pain. 2003; 105: 17-25Abstract Full Text Full Text PDF PubMed Scopus (317) Google Scholar, 24Pitz M. Cheang M. Bernstein C.N. Defining the predictors of the placebo response in irritable bowel syndrome.Clin Gastroenterol Hepatol. 2005; 3: 237-247Abstract Full Text Full Text PDF PubMed Scopus (102) Google Scholar A more recent systematic review and meta-analysis found higher placebo rates in European randomized controlled trials (RCTs) compared with those conducted in other continents; in those that used physician-reported outcomes compared with those that used a patient-reported end point; and in RCTs using shorter duration of therapy.25Ford A.C. Moayyedi P. Meta-analysis: factors affecting placebo response rate in the irritable bowel syndrome.Aliment Pharmacol Ther. 2010; 32: 144-158Crossref PubMed Scopus (160) Google Scholar Also, pooled placebo response rates were generally higher in RCTs using clinical criteria to define the presence of IBS compared with those using Rome criteria, trials using 3 times daily dosing, trials that assigned patients to placebo or active therapy in a 1:1 ratio, trials of antispasmodics and mixed 5-HT3 antagonists/5-HT4 agonists, and trials of lower scientific quality.25Ford A.C. Moayyedi P. Meta-analysis: factors affecting placebo response rate in the irritable bowel syndrome.Aliment Pharmacol Ther. 2010; 32: 144-158Crossref PubMed Scopus (160) Google Scholar In contrast to placebo, nocebo (from the Latin “I shall harm”)20Bernstein C.N. Placebos in medicine.Semin Gastrointest Dis. 1999; 10: 3-7PubMed Google Scholar is the expectation of distress. The expectation of side effects may increase the frequency with which adverse effects are reported in both the active and control arms of a drug study, and may increase the likelihood that subjects will drop out of the trial. The term precebo was coined to describe the effect that influences placebo even before the study begins.26Kim S.E. Kubomoto S. Chua K. et al.“Pre-cebo”: an unrecognized issue in the interpretation of adequate relief during irritable bowel syndrome drug trials.J Clin Gastroenterol. 2012; 46: 686-690Crossref Scopus (12) Google Scholar The precebo effect refers to the potential for a drug benefit during a clinical trial to be influenced by preconceived notions or by communications about the trial contained in advertisements and consent forms. A period of prospective baseline measurement before treatment is useful to evaluate patient eligibility. This also limits recall and reporting biases and ensures that patients are currently symptomatic. It allows comparison of patients in the active and placebo groups, as well as evaluation of a clinically important change in health status. Older studies have used a placebo run-in period where all patients received placebo for a specified period and their responses were assessed using the study outcome measures. Patients who significantly improved were excluded. Although acceptable to regulatory agencies, placebo run-in can underestimate the overall effect size.27Berger V.W. Rezvani A. Makarewicz V.A. Direct effect on validity of response run-in selection in clinical trials.Control Clin Trials. 2003; 24: 156-166Abstract Full Text Full Text PDF PubMed Scopus (51) Google Scholar The double-masked, randomized, placebo-controlled, parallel-group trial is the gold standard for testing the efficacy of new treatments. Variations of this basic design include different groups receiving different doses of the active treatment (dose-ranging, in phase 2), more than one control treatment, multiarm trials, a baseline period of no treatment, and a washout period after treatment is completed. As there is no universally effective treatment for any FGID, the standard approach is to test a new therapy against placebo to prove its superiority. Occasionally, trials of equivalence and noninferiority are performed where a new therapy is more convenient or less expensive.18Temple R.J. When are clinical trials of a given agent vs. placebo no longer appropriate or feasible?.Control Clin Trials. 1997; 18 (discussion 661−666): 613-620Abstract Full Text PDF PubMed Scopus (50) Google Scholar Crossover designs have been popular in FGID treatment trials.6Spiller R.C. Problems and challenges in the design of irritable bowel syndrome clinical trials: experience from published trials.Am J Med. 1999; 107: 91S-97SAbstract Full Text Full Text PDF PubMed Scopus (149) Google Scholar Subjects receive both treatments during distinct time periods, usually separated by a washout phase, in randomized order, with the aim of comparing the treatments. Theoretically, a crossover design can increase sensitivity to detect change, allowing a smaller sample size for the desired statistical power. However, there are down sides: patient dropout and missing data have a greater impact than in a parallel-group design, carryover effects that occur when the first treatment influences the response to the second treatment, and there is a higher risk of unmasking due to side effects. Therefore, crossover trials seems most applicable in physiological studies where end points are objectively measured. A factorial design is appropriate when evaluating combination treatments, which may be desirable in patients with severe FGID symptoms.28Drossman D.A. Camilleri M. Mayer E.A. et al.AGA technical review on irritable bowel syndrome.Gastroenterology. 2002; 123: 2108-2131Abstract Full Text Full Text PDF PubMed Scopus (1201) Google Scholar This requires a control group for each intervention. The withdrawal trial is an “enrichment design” in which all subjects receive the active treatment and, at a predefined time point, are classified as responders or nonresponders. The latter are then excluded and responders are randomly assigned to continue with treatment or placebo. The efficacy assessment is based only on the second part of the trial. Potential carryover effects from active treatment are the major drawback.29Silvers D. Kipnes M. Broadstone V. et al.Domperidone in the management of symptoms of diabetic gastroparesis: efficacy, tolerability, and quality-of-life outcomes in a multicenter controlled trial. DOM-USA-5 Study Group.Clin Ther. 1998; 20: 438-453Abstract Full Text PDF PubMed Scopus (126) Google Scholar In trials evaluating the efficacy of behavioral, surgical, or many types of complementary and alternative medicine interventions, it is not possible to mask the intervention from the therapist (the individual implementing the intervention) or from the patient. Expectation of benefit is the most important variable to balance across intervention arms. Some published trials of behavioral interventions have compared symptom improvement in the active treatment group to symptom changes in people who remain on a waiting list to receive the intervention or who continue to receive “standard medical care.” However, both of them create a negative expectancy of improvement and therefore have potential to overestimate the efficacy of the investigational treatment. A better approach is to identify an alternative, active treatment that generates a similar expectation of benefit and is assumed to be less effective. Investigators have also tried to balance the amount of contact time with the therapist and other characteristics across treatment arms.30Heymen S. Scarlett Y. Jones K. et al.Randomized controlled trial shows biofeedback to be superior to pelvic floor exercises for fecal incontinence.Dis Colon Rectum. 2009; 52: 1730-1737Crossref PubMed Scopus (160) Google Scholar, 31Rao S.S. Seaton K. Miller M. et al.Randomized controlled trial of biofeedback, sham feedback, and standard therapy for dyssynergic defecation.Clin Gastroenterol Hepatol. 2007; 5: 331-338Abstract Full Text Full Text PDF PubMed Scopus (283) Google Scholar The expectation of benefit should be measured in both groups to confirm that the treatment arms are balanced.14Devilly G.J. Borkovec T.D. Psychometric properties of the credibility/expectancy questionnaire.J Behav Ther Exp Psychiatry. 2000; 31: 73-86Crossref PubMed Scopus (1298) Google Scholar A number of" @default.
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• W2065994042 title "Design of Treatment Trials for Functional Gastrointestinal Disorders" @default.
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