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Design of Treatment Trials for Functional GastrointestinalDisorders Design of Treatment Trials Committee: E. JAN IRVINE,* WILLIAM E. WHITEHEAD,‡WILLIAM D. CHEY,§ KEI MATSUEDA,ʈ MICHAEL SHAW,¶ NICHOLAS J. TALLEY,#,** andSANDER J. O. VELDHUYZEN VAN ZANTEN‡‡*Division of Gastroenterology, St. Michael’s Hospital and University of Toronto, Toronto, Ontario, Canada; ‡Division of Gastroenterology,University of North Carolina–Chapel Hill, Chapel Hill, North Carolina; §Division of Gastroenterology, University of Michigan, Ann Arbor,Michigan; ʈDivision of Gastroenterology, NCNP, Ichakawa City, Japan; ¶Division of Gastroenterology, Park Nicollet Clinic and University ofMinnesota, Minneapolis, Minnesota; #Division of Gastroenterology, Mayo Clinic College of Medicine and Division of Gastroenterology andHepatology, Rochester, Minnesota; **Department of Medicine, University of Sydney, Sydney, Australia; and ‡‡Division of GastroenterologyDalhousie University, Halifax, Nova Scotia, Canada This document addresses the design of trials to assess the provide standards to help explain the mechanisms of efficacy of new treatments for functional gastrointestinal therapeutic success and enable regulatory agencies, re- disorders (FGID), emphasizing trials in irritable bowel syn- searchers, and providers to better evaluate the quality of drome and dyspepsia, because most research has been published studies. This report focuses largely on designs undertaken in these conditions. The double-blind, random- that evaluate treatment efficacy, with emphasis on irri- ized, placebo-controlled, parallel group trial remains the table bowel syndrome (IBS) and functional dyspepsia preferred design. Randomized withdrawal designs, al- (FD), because they have been studied most extensively.
though encouraged by the European Agency for the Eval- Studies that address pathophysiology or mechanism of uation of Medicinal Products, have the same potentialdisadvantages as a crossover design, including carryover treatment effects are not included in this review because effects, unmasking (unblinding), and overestimation of the they require quite different and diverse study designs.
potential benefit for clinical practice. Innovative trial de- Recommendations in this article are based largely on signs that evaluate intermittent (on demand) treatment consensus of the literature, except where specifically in- are likely to become more common in the future. Investi- dicated. We refer readers to the corresponding chapter in gators should include as broad a spectrum of patients as the Rome III book for a more detailed discussion with possible and should report recruitment strategies, inclu- sion/exclusion criteria, and attrition data. The primaryanalysis should be based on the proportion of patients in each treatment arm who satisfy an a priori treatment responder definition, or a prespecified clinically meaningfulchange in a patient-reported symptom improvement mea- The goals of most treatment trials are to ascertain sure. Such measures of improvement are psychometrically the impact of the intervention(s) on (1) the frequency and validated subjective global assessments or a change from severity of symptoms, (2) health status and quality of life, baseline in a validated symptom severity questionnaire. It (3) the patient’s ability to cope with symptoms, and/or is unethical to change the responder definition after a trial (4) the use of health care resources. Generally, a single begins. Data analysis should address all patients enrolled, using an intention-to-treat principle. Reporting of results Investigators should select their most important research ques- should follow the Consolidated Standards for ReportingTrials guidelines and include an analysis of harms data and tion(s), pertinent to the specific FGID, develop a hypothesis secondary outcome measures to support or explain the based on available evidence, and design a study that will most primary outcome. Trials should be registered in a public effectively answer the proposed research question. location, prior to initiation, and should be published even ifthe results are negative or inconclusive.
Abbreviations used in this paper: CONSORT, Consolidated Standards for Reporting Trials; EMEA, European Agency for the Evaluation ofMedicinal Products; FD, functional dyspepsia; FGID, functional gastro- Thecommittee’saimsweretoreviewtheliteratureon intestinal disorder; ITT, intention to treat; NNH, number needed to trial design for the functional gastrointestinal dis- harm; NNT, number needed to treat; IBS, irritable bowel syndrome.
2006 by the American Gastroenterological Association Institute orders (FGIDs), to further develop to assist researchers in conducting treatment trials for the FGIDs, Special recruitment strategies such as advertising have been accepted in some countries to accelerate recruit- A broad spectrum of patients should be included to ment. A recent IBS study observed that patients re- support the generalizability of the trial findings to patients cruited by newspaper advertisement, in comparison to outside of the trial. In pharmaceutical research, particularly, patients enrolled by gastroenterologists, were older, more regulatory agencies may limit licensed drug indications to highly educated, more often depressed but less anxious, the trial population. The study population should be se- and had less severe IBS symptoms; primary care patients lected based on the question, treatment (including possible were also anxious but had symptom severity that was side effects), expected results, and empirical A screen- intermediate between patients recruited by advertise- ing log, summarizing the most important demographic ment and patients recruited from gastroenterology clin- variables in patients entered or excluded and the reasons for Recruitment strategies should be clearly identified to allow A screening log provides support for the generalizability of the exploration of different patterns of treatment response. Specified inclusion and exclusion criteria are manda- tory for all studies and should include the FGID case Important patient characteristics to report include definition. If enrollment is targeted to a special popula- age, gender, race, symptom severity, duration of disease, tion to maximize treatment efficacy or minimize side prior treatments for the study condition (and response), and the use of coexisting medications, including over- It is advisable to include as broad a spectrum of patients as the-counter drugs and vitamins. These may impact out- possible, defined by the ROME-specific FGID criteria. Restrict- comes and should be tested as possible disease or effect ing the study population must be justified and inclusion and modifiers. For example, gender differences in drug re- exclusion criteria must be specified. sponse have become evident in clinical trials of certain In clinical practice, many physicians avoid formal serotonergic drugs in patients with Depending on investigation in favor of a positive diagnosis, reassurance, the hypothesis, investigators may choose to enroll only and lifestyle modification. However, entry criteria for one gender. However, if both women and men are to be treatment trials must be more specific. The consensus included, there should be sufficient numbers of both to view is that the minimum evaluation should include a allow meaningful subgroup analyses. As data accumulate complete blood count, imaging of the relevant part of the describing the genetics of the FGIDs in relation to drug gastrointestinal tract within the previous 5 years, and responsiveness, it may become relevant to assess these other investigations determined by symptoms and family parameters during clinical It is also advisable to Emerging evidence suggests that screening IBS assess for psychological distress or prior mental health patients for gluten enteropathy may also be problems; in trials of psychological interventions or psy- When testing is required for study inclusion, it should choactive drugs, these may be important effect modifiers, be consistent across all study arms, and the timing and in trials of nonpsychological treatments, they are potential confounders that could influence both baseline The minimum screening investigation for eligibility should be Potential disease modifiers/confounders that might affect re- Most trials of FGIDs have been conducted in academic sponse to therapy should be assessed. centers specifically interested in the FGIDs, creatingconcerns of selection bias that favor inclusion of patientswith more severe symptoms and/or with psychosocial Two large trials showed significant differences in Clinical trials differ from usual practice in several treatment response between primary and referred pa- ways, including the application of strict eligibility cri- tients with Thus, researchers should consider re- teria, use of a placebo, a standardized intervention, fre- cruiting broadly, noting if subjects are from primary, quent follow-up visits with extensive data recording, and secondary, or tertiary care. Differences in baseline sever- the use of study coordinators. Nonetheless, standard ity and treatment response by site or type of recruitment aspects of diagnosis and management, especially an ad- equate explanation and reassurance about the disease, are Patient characteristics should be documented sufficiently to part of standard care and should be provided to all examine the comparability of patients among centers and allow patients in the trial. Novel interventions must show comparisons with other populations. promise of a benefit over standard care.
or drug trials in which the active drug causes predictable side effects or rapid symptom change, are difficult tomask from patients or investigators, but possible solu- tions to maintain an investigator-masked outcome assess- ment include using independent assessors who are un- interviewer or self-administered questionnaire, or per- forming laboratory tests (eg, anal manometry in fecal incontinence) that are interpreted by individuals not It is mandatory to undertake the maximum masking possible, determined by the type of intervention and study design. Randomization. Randomization is a process (equiv- alent to the flip of a coin) used to assign patients to treatment arms in an unbiased fashion. The allocation se- quence should be concealed from investigators and research personnel should be unaware of the treatment to which a patient will be assigned until after the patient has beendeemed eligible and has consented to Stratifiedrandomization, whereby the most important prognostic fac- Every trial should incorporate the principles of good clinical tors (eg, gender and usual bowel habit) are identified be- practice to ensure that the study results are relevant to real forehand, uses a separate randomization sequence for each stratum (eg, male versus female or constipation-predomi-nant versus diarrhea-predominant IBS) to balance these factors among treatment Stratification should be limited to 1 or 2 fParticularly in multicenter Study designs for treatment trials in FGID face trials, in which sites may enroll only a few subjects, ran- several important challenges: (1) a high placebo response domization can be performed in blocks. A block refers to the number of subjects within which the group assignments for multimodal therapy owing to weak effects of available have to be balanced. A permutated block design (variable block treatments or multiple etiologic mechanisms interacting size) ensures that the sequence of assignments is unpredict- in the disease (4) difficulty of masking (blind- able to the investigator. When reporting the trial, the ing) patients and investigators, particularly in trials of randomization procedure should be explicitly described be- cause it is a potential source of bias.
the-counter treatments or drugs taken for other condi- Investigators must include a detailed description of their tions (eg, antidepressants); and (6) avoidance of harms in randomization scheme in the report of the study. Selecting the control group. A placebo control Bias, defined as systematic error that leads to a devi- group is essential to establish the efficacy of a new ation of the estimated treatment effect from its true treatment. When a proven efficacious treatment exists, value, may enter a clinical trial at any stage from patient comparison against this active treatment may be consid- enrollment to publication of the results. The major but inclusion of a placebo is still recommended to avoid an inconclusive trial, in which the active treat- Masking. Double masking (of both patients and researchers) to the intervention ensures the validity of the Behavioral therapy pose particular challenges outcome assessment. “Triple masking” is desirable and to identify inactive comparison treatments that generate extends masking to all investigators, including data expectancy comparable to the active intervention. Un- managers and In drug trials, investigators treated patients are poor control subjects because they are encouraged to ask both the patient and the interven- tionist who interacts with the patient at the end of the result in an overestimate of the impact of the interven- trial whether they believe the active treatment was ad- tion. Options to assess the integrity of behavioral trials ministered and to report these data. Certain interven- include (1) testing the credibility of both active and tions, such as psychotherapy, hypnosis, sphincterotomy, control interventions after initial exposure (eg, by using the Credibility or (2) using a process measure The placebo response rate in treatment trials of FGIDs is to ensure that the active treatment is producing the substantial and largely unavoidable. intended effects on physiology or cognitions while the Baseline observation versus placebo run-in. A control treatment does not (eg, does biofeedback for fecal period of prospective baseline measurement before treat- incontinence change anal sphincter squeeze pressure ment is useful to evaluate patient eligibility. This also more than the control condition, or does cognitive– limits recall and reporting biases by ensuring that pa- behavioral therapy alter the patients dysfunctional atti- tients are currently symptomatic. It allows comparison of tudes to a greater extent than an education control patients in the active and placebo groups, as well as evaluation of a clinically important change in health sources of bias and their potential impact on study findings in the discussion section of the report.
Older studies have used a placebo run-in period where A placebo control group is essential. In behavioral treatment all patients received placebo for a specified period and trials, confirming that the control condition produces a similar their response was assessed, using the study outcome expectation of benefit, but does not act on the same physiologic or measures. Patients who significantly improved were ex- psychological principles, is recommended. cluded from further participation to reduce the propor-tion of placebo responders and to exclude patients with poor adherence. This has been used in several trials of A placebo is an intervention believed to lack any allergic rhinitis and, although acceptable to regulatory specific effect to change a particular Placebo agencies, may underestimate the overall effect It effects range from 10% to 70% for and 0% to 84% is also difficult to predict whether (1) the placebo re- for This substantial placebo response rate makes it sponse increases, plateaus, or decays after the run-in more difficult to demonstrate superior efficacy of new (2) a differential dropout occurs, and (3) patients treatments. Of note, a placebo administered by a physi- removed from a trial have a different response to those cian appears to be more powerful than one given by other who continue. Exclusion of patients for placebo response may also disrupt the doctor–patient relationship for fu- an order effect, in which an effective drug has a lesser benefit when given after a placebo. This is especially The disadvantages of a placebo run-in appear to outweigh the important if a placebo run-in period is implemented to benefits and it is best avoided. However, baseline observations exclude placebo responders or in studies with a crossover design, because approximately half of patients in a cross- External factors may also contribute to changes in The double-masked, randomized, placebo-con- health status making it difficult to detect a treatment trolled trial is the gold standard method to test the effect, including (1) a natural variation in symptoms, (2) efficacy of a new treatment. A parallel group study regression toward the mean, and (3) unidentified or design requires that patients be randomized to receive unintended cointerventions. Regression to the mean is the only one treatment assignment throughout the trial (af- likelihood that patients consult when symptoms are par- ter a period of baseline assessment without treatment).
ticularly severe and improve with time owing to the Dose-ranging studies (different groups receive different natural variation in symptom severity and irrespective of doses) and multiple control treatments, with a baseline observation of no treatment or a washout period after changes in diet or using over-the-counter remedies could treatment, are different variants of a parallel group de- also lead to a false interpretation that an intervention was effective, as could the extra attention given patients by Crossover designs, in which subjects receive both treat- researchers during clinical trials (Hawthorn The ments during distinct time periods, separated by a wash- magnitude of the placebo response may also be influ- out phase have been popular in some FTheoret- enced by the wording of the question used to define ically, lesser variability in outcomes within subjects treatment response or by the use of a compound ques- could require a smaller sample size for the desired sta- tistical power. However, patient dropout rates and miss- the placebo response rate is larger when a responder is ing data have a greater impact than in a parallel design, defined by a global improvement in IBS symptoms com- because patients are omitted from both study arms when pared to defining a responder by reduction in abdominal data are missing. The greatest disadvantages of crossover pain (average placebo responses of 36% versus 28%).
designs are (1) the carry-over (period-by-treatment) ef- fects that occur when the first treatment influences the There is a growing interest in developing drugs for response to the second treatment or when symptoms intermittent treatment (short-course administration for a change with and (2) the high likelihood of un- predetermined time period after symptom recurrence) or masking owing to side The European Agency on-demand treatment (medication is taken only during for the Evaluation of Medicinal Products (EMEA) may symptoms). These issues have been addressed in gastro- accept a crossover design for a Phase III trial, yet has esophageal reflux IBS and FD trials have fo- highlighted problems that could invalidate study re- cused on continuous administration of drugs to moderate and does not provide guidance for analysis. If period and sequence effects occur, only the first treat- ment period data should be used to determine efficacy.
believe that patients often take medications only as Although crossover designs are not recommended for needed. Trial designs and outcome measures required for treatment trials with subjective end points, they may be testing the efficacy of intermittent therapy differ from used in physiologic studies, where the end points are those used to test continuously administered treatments.
After establishing efficacy during continuous administra- A factorial design can be undertaken to evaluate com- tion, intermittent or on-demand studies can be con- bined For example, to test the effects of ducted. Guidelines for intermittent treatment of mi- combining two treatments, A and B, subjects are ran- domly assigned to 4 groups: no A and no B; A and no B; B and no A; or both A and B. Investigators might The parallel group design is the accepted standard for consider such a design either (1) to save money by testing evaluation of efficacy for most treatments and is applicable to 2 treatments at once with fewer subjects overall, or (2) to most experimental situations. The crossover design is best test for synergistic effects of combined treatments. Im- portantly, the 2 treatments should have distinct mecha- Types of trials. The strongest case supporting the nisms of action to be able to interpret the simple effects efficacy of a new medication is made by demonstrating (ie, the comparison of all patients receiving treatment A clinical and statistical superiority to placebo or an active to all patients not receiving treatment A, and the com- control treatment. An equivalence study or noninferior- parison of all patients receiving treatment B to all pa- ity trial can also be considered if (1) a known, effective tients not receiving treatment B), or to detect whether treatment is available and it would be unethical to there is added benefit from combining treatments. Also, administer a placebo (eg, cancer or inflammatory bowel a control is required for each intervention. Potential cost disease, not FGID), or (2) a new treatment might be less savings are frequently offset by the complexity of inter- costly, safer, or just as good as standard Such preting the data, except when testing for synergistic trials are usually more costly than superiority trials, because much larger sample sizes are required. Investi- The withdrawal trial is an enrichment design, in which gators must first estimate the expected difference be- all subjects receive the active treatment. At a predefined tween standard treatment and placebo from a meta- time point, they are classed as responders or nonre- sponders and the latter are excluded. Responders are then “equivalence margins” that are smaller than the expected randomly assigned to receive active treatment or placebo difference. The trial is judged to be positive only if the and efficacy is based on the second part of the trial.
95% confidence interval for the observed difference be- Potential carry-over effects from the first treatment, how- tween the new and standard treatments falls within the ever, can prevent an accurate estimate of the drug benefit.
equivalence margins. For a noninferiority trial, only the lower 95% confidence limit must fall within the drugs for short-term efficacy in IBS, and require 2 or more treatment cycles to demonstrate efficacy. The In trials that compare the investigational treatment to a different active treatment, the investigator is obliged to placebo at an unpredictable time) be undertaken after show that the treatment arms are in equipoise; it is active drug, but does not address how to perform the unethical, for example, to compare the investigational complex statistical analysis. Like the placebo run-in, this drug to an ineffective dose of an alternative compound.
design can overestimate the effect One completed Superiority trials (not equivalence or non-inferiority trials) followed the EMEA guidelines (with minor vari- ations) and provided data supporting the efficacy of Duration of treatment. Treatment duration for tegaserod for IBS on repeated dosing cycles.
specific FGIDs should be based on natural history data describing the frequency and duration of episodes. For IBS, this is highly but for the majority of Diaries have been used to measure primary or patients both flares and remissions appear to last less than secondary end points and minimize recall bias. Relatively 1 wfor dyspepsia, there is a high symptom few symptoms are recorded and ratings can be performed at a fixed time (eg, bedtime) or when symptoms actually dations for trials of 8 –12 weeks were based on experience occur. The former method is simpler for data analysis. A and on concerns for cost and ability to retain patients.
major problem of is poor adherence; patients EMEA differentiate trials of short-term ef- often complete them retrospectively or just before a ficacy, for which they would accept 4-week trials, from Hand-held electronic devices with reminder long-term efficacy trials, for which 6-month trials are required. Although both types of trials require patients been shown to improve adherence to 80%–90%, and with active symptoms at randomization, long term-stud- patient satisfaction is Diary symptoms can also ies could include patients with intermittent symptoms.
be recorded on secure Web sites, which can accurately Further research on the natural history of individual FGIDs should be a high priority, to allow clearer recom- Retrospective questionnaires are an acceptable method for mendations for trial duration. Extended follow-up assessing symptoms provided the recall interval is limited to 3 should be considered to determine treatment durability months. Patients should receive clear instructions on the use of a and should relate to symptom periodicity and presumed diary, including the directive to leave it blank if they forget to record information. Electronic diaries are preferred over paper A minimum treatment duration of 4 weeks that reflects the diaries. Methods to ensure adherence to recording methods should symptom periodicity and anticipated treatment mechanism is recommended. If chronic use is anticipated, trials of at least 6months should be undertaken to establish long-term efficacy. Adherence to treatment and study protocol. Stan- The primary outcome variable(s) provides the ba- dard methods to assess adherence include interviewing sis for judging the success or failure of an intervention.
Only 1 or at most 2 variables should be selected and this blood levels of and may be especially im- should be done before the trial begins. The Food and portant when interpreting studies of long duration. The Drug Administration and EMEA have recommended frequency of missed or late appointments and missing that investigators provide rules, a priori, that allow clas- data from diaries or questionnaires should be reported for sification of each participant as a responder or nonre- Adherence to the protocol and treatment should be measured. include secondary outcome variables to (1) strengthenthe results by showing concordance between individualsymptoms and the primary outcome measure, (2) address the mechanism of the intervention, (3) assess the safety or (4) cost effectiveness of the treatment, and (5) identify variables that predict which patients are most or leastlikely to benefit.
Efficient symptom assessment can be achieved by The definition of a responder should reflect a clinically having patients complete questionnaires before treat- meaningful symptom improvement for each patient. For ment and at follow-up visits. However, concerns about IBS and other FGIDs, there is no consensus on what the accuracy of retrospective questionnaires include constitutes a clinically meaningful improvement. Some whether (1) symptoms present on the day they complete studies accept as little as a 10% reduction in a visual the questionnaire influence reporting; (2) poor recall analog scale rating of symptom or 1 step on a affects the accuracy of a retrospective report; and (3) 7-step ordinal as clinically meaningful, whereas patients feel pressured to give a more positive report if other studies require a 50% reduction in an aggregate questionnaires are completed in the presence of the in- vestigator. Although data support the presence of these the most commonly employed definition of clinically biases, they do not appear to be Recall of meaningful improvement in IBS has been a patient’s health-related events appears to be reasonably accurate report (yes or no) of “adequate relief of abdominal pain and or “satisfactory relief of IBS symp- These definitions are assumed to have face Adequate relief or satisfactory relief as a primary validity. However, empirical data are needed for each outcome measure. Since 1999, most published pharma- outcome measure to assess the clinical significance of ceutical trials for IBS have used “adequate relief of ab- different degrees of change from both the patient’s and dominal pain and or ”satisfactory relief of IBS as their primary outcome measure.
One or at most 2 primary outcome measures should be specified Responders were defined as patients who reported “yes” in advance. Investigators should list criteria to classify each to adequate relief or satisfactory relief on at least half of patient as a responder or nonresponder based on a clinically the weeks in the treatment trial. These studies demon- strated statistically significantly higher responder ratesfor active drug relative to placebo and led to approvals for alosetron and tegaserod by the Food and Drug In selecting a primary outcome, investigators should examine the trial objectives, population, and Mangel et assessed the validity of the adequate mechanism of action of the proposed treatment and relief measure in diarrhea-predominant IBS patients and should choose either a global measure, which integrates showed that responders differed significantly from non- the symptoms into a single numerical index, or the responders regarding pain-free days, pain severity, ur- summary score of a validated symptom severity and/or gency, stool frequency, and 6 of 8 SF-36 quality of life subscales plus 8 of 9 scales on a disease-specific quality of Attention should be paid to the suitability of the life measure. However, correlations among measure- measurement scale used for each outcome measure. A ments (convergent validity), test–retest reliability, and detailed discussion of measurement scales and their prop- internal consistency were not reported. Similar validation erties is beyond the scope of this report, but is more data have been reported for satisfactory thoroughly addressed in the Rome III book and else- Integrative symptom questionnaires. An alterna- tive method for defining a responder in an IBS treatment Physician-reported assessments have been accepted in trial is to ask patients to report the frequency or severity some but are subject to greater measurement of all (or a representative group) of IBS symptoms prior error than patient Therefore, patient-reported to and again following treatment, and to define a re- measures are endorsed. Only fully validated instruments sponder as a patient who reports at least a 50% decrease are recommended as primary outcome assessment tools, and secondary outcome measures should also be assessed tionnaires that examine the severity of IBS, such as the for robustness. Psychometric validation requires that (1) Gastrointestinal Symptom Rating Scale for and the the assessment instrument includes symptoms relevant Functional Bowel Disorder Severity However, to and fully representative of the disorder (face validity);(2) it show a predictable relationship with other measures the Irritable Bowel Syndrome Symptom Severity (construct validity); (3) the assessment produces similar is the only IBS symptom severity scale that has been results when readministered to patients whose health status has not changed (reliability); (4) it can detect Whitehead et compared different outcome mea- clinically meaningful change in health status when such sures including satisfactory relief and a 50% reduction in a change has occurred (responsive); and (5) changes in score the Irritable Bowel Syndrome Symptom Severity Scale can be related to clinical indicators that are meaningful questionnaire, in an observational study of patients’ re- to clinicians (criterion validity).
sponse to usual medical care for IBS. They reported that Validation of a new outcome measure is best estab- the response rate on satisfactory relief was influenced by lished in a separate The frequency of data re- pretreatment symptom severity: patients with initially cording for each outcome should also be specified before mild IBS symptoms showed the highest responder rate the trial begins, as should the time frame defining the but the smallest change in symptom severity, whereas patient response (whether at the end of the trial, during patients with initially severe IBS symptoms showed the a prespecified proportion of weeks or months that re- lowest responder rate but the largest decrease in severity.
sponder criteria have been fulfilled, or for all time points In contrast, when defining a responder as a patient who reported at least a 50% decrease in symptom severity, A patient-reported outcome assessment is recommended. Psy- pretreatment symptom severity had no impact on the chometric validation of each outcome measure is recommended responder rate. Defining a responder based on a 50% before it is used in clinical trials. reduction in symptoms has been used in several stud- how they were measured. Investigators should attempt to ever, like satisfactory relief and adequate relief, it re- place benefits and harms for any intervention into Subjects can be classed as responders and nonre- Anticipated and unanticipated adverse events should be sponders at different time points during a trial. In pub- lished trials, patients were classified as responders if theyreported adequate relief or satisfactory relief on at least The reasons for including each secondary outcome However, this loses important information; the most and the plan for analysis should clearly be identified persuasive evidence for efficacy would be to show that before the trial begins. Health economic outcomes are patients in the active treatment had a sustained response becoming an important class of secondary once they reported satisfactory or adequate relief. Inves- Secondary outcomes should be selected based on the study tigators are encouraged to use more sophisticated statis- question and should be validated measures that support or tical models that address the longitudinal trajectory of explain the results. Integrating health economic outcomes is report the proportion of patients responding at each time Quality of life assessment. FGIDs significantly impact quality of Generic and disease-specific Several well-validated outcome measures have been quality of life instruments are Generic in- used in FD These use a single global outcome of struments can assess quality of life in large populations a specific symptom (eg, Glasgow Dyspepsia Severity and across a wide spectrum of disorders, but may not a global overall assessment of dyspepsia symp- reflect all important aspects of health status for specific toms (eg, the Canadian Dyspepsia the LEEDS disorders. They may be less sensitive to detect important treatment effects, but they permit comparisons with important dyspepsia and quality of life outcomes (eg, the other diseases and help to detect unexpected changes in health status after treatment. Examples of validated in- struments include the Sickness Impact the Nottingham Health Profile, the SF-36 (Short Form of outcome measures are yet to be developed.
General Well-Being Disease-specific quality of Pain or discomfort is a key feature of many FGIDs and is typically either the primary outcome variable or an FGID (eg, the fear of fecal incontinence in IBS). Theo- important secondary outcome variable in clinical trials.
retically, they can detect smaller and more specifically Pain has 3 dimensions—intensity, duration, and fre- relevant changes in health status, which may be missed quency—that can be considered separately or integrated by generic instruments. Quality of life measures have not in a global assessment of pain or can be incorporated into been used as the primary outcomes in pharmaceutical a quality of life measure. Different rating scales can be clinical trials because they were believed to be insuffi- used that are reproducible and sensitive to If ciently responsive to treatment, but have been strongly pain is chosen as the primary outcome, a meaningful recommended as secondary outcome variables. One re- clinical response should be defined beforehand, and the port focusing on the health-related quality of life data proportion of patients reaching this end point reported.
from two previously reported trials of alosetron found a Adequate relief and satisfactory relief are the current stan- significantly greater improvement on active drug com- dards for primary outcome assessment in treatment trials in pared to challenging the belief that these FGIDs. Alternative outcome measures such as integrative symp- measures are not responsive enough to be employed as tom questionnaires are also acceptable. All of these measures Quality of life assessments are important secondary outcomes. Safety issues and absence of harms. Every trial Investigators are encouraged to include both a baseline generic should document and report adverse events. Recent at- and a pre–post disease-specific quality of life instrument. tention has focused on the appropriate reporting ofharms-related issues in randomized clinical When collecting harms data is a trial objective, it shouldbe reflected in the manuscript reporting the study results The type of statistical analysis is determined by and the report should clearly define adverse events and the particular study design and primary outcome mea- sure(s). The Consolidated Standards for Reporting Trials efficacy trial, can also allow computation of the number (CONSORT) statement was developed by scientists and of patients who need to be treated (NNT) to encounter a editors to improve the quality of reporting parallel patient who will experience a clinical benefit. Although group, randomized, controlled It emphasizes the the NNT is reported infrequently in randomized, con- importance of transparently reporting the study objective trolled trials, its inclusion can convey the clinical impor- and how the study was conducted and analyzed. Evidence tance of a study Similarly, harms data can be supports improved quality of methodology and data used to estimate the number of patients that would need to be treated with a drug to see an adverse event (number journals now require that manuscripts describing clinical needed to harm [NNH]). Calculation of the NNT and trials conform to the CONSORT guidelines, found on NNH allows the researcher or clinician to more quanti- tatively assess the benefits and risks of any given therapy.
tions have made similar recommendations for studies When reporting P values, actual values and not thresholds evaluating diagnostic testing (Standards for Reporting of should be provided. An NNH can be calculated based on the risk of adverse effects and can be weighed against the NNT. analyses (Quality of Reports of Meta-Analyses state- The statistical analysis should be based on an inten- tion-to-treat (ITT) with a plan for handling Investigators should adhere to the CONSORT statement on dropouts. The trial can either be analyzed as the propor- tion of responders in each group, treating all dropouts as The main analysis for FGID trials should focus on the nonresponders, or by carrying forward the last observa- primary outcome measure(s) to determine whether or not tion available for the primary outcome. A dual analysis, the study results support a new treatment. Although the examining for differences in results using the 2 different main outcome often compares the end of treatment and methods should be performed. Many studies also report baseline observations, data should also describe how pa- a per protocol (all patients who followed the protocol) or tients changed during the study; the results of a trial are an all-patients-treated (all patients who received treat- far more compelling if patients have had a sustained ment following randomization) analysis. These analyses response to the intervention. When 2 primary outcome may provide insight as to whether a treatment works variables are included in a trial, investigators should under optimal conditions, but cannot replace the ITT specify in advance whether the trial will be considered analysis. When there is a discrepancy between the ITT positive if only 1 outcome measure is significant, or if (negative) and per protocol (positive) analyses, the results both are required. If significance on any primary outcome should be interpreted as inconclusive. The effect of po- suffices, the analysis should adjust for multiple compar- tential modifiers such as gender, age, duration or severity isons, for example, using the Bonferroni of disease, and presence of psychological stress can be The committee suggests that the EMEA recommenda- assessed using a logistic regression analysis, where the tion requiring 2 positive primary outcomes for trials in binary dependent variable represents the a priori speci- IBS may be overly conservative. The primary outcome fied definition of a Such covariates should results should be stated in absolute numbers to include both a numerator and denominator; it is not sufficient to The primary analysis should be the ITT analysis and must list only percentages of (non)-responders (eg, not 20% but rather 10/50, 20%). For all outcome measures, theestimated effect of the intervention (difference between active and placebo treatment) and a 95% 2-sided confi- The main result of the study must be based on the evaluation Results should be reported for all prespecified of the primary outcome measure as stated in the protocol before outcomes. Score changes should be reported for each the study begins. The primary outcome should be stated in cardinal symptom of the entry criteria. Secondary absolute numbers and should include a 95% confidence interval. outcomes that are used to support or refute the pri- Statistically significant differences between study mary analysis should be analyzed by ITT and not per groups can also be expressed using a P value. Actual protocol. Adjustment for multiple comparisons is gen- values and not thresholds (ie, not P Ͻ .05) should be erally unnecessary when analyzing secondary outcome provided and should be complementary to confidence measures because the efficacy of the treatment is intervals. The reciprocal of the absolute risk reduction, in judged on the basis of the analysis of the primary a risk reduction trial, or therapeutic gain, in a treatment outcome variable, not the secondary outcomes. Sec- ondary outcome measures are examined to support the primary outcome analysis. When many secondary vari- There is no compelling reason to incorporate in- ables are included to identify predictors of response or terim analyses in trials to determine efficacy because explore for other benefits, the type I error rate may be FGIDs are not life threatening. Moreover, because the incidence of serious adverse events is expected to be low, any occurrence of a serious adverse event is likely to increase the likelihood of a type II statistical error, prompt the safety committee to reevaluate the trial with- rendering truly important differences nonsignificant.
out carrying out an interim analysis. Thus, interim anal- Using descriptive rather than inferential statistics (eg, yses in trials of FGIDs are normally only done to assess means and confidence intervals) or reporting actual P the futility of continuing the trial. Plans for interim analyses should be clearly prespecified in the study pro- Specific plans to present and analyze harms data tocol and appropriate statistical methods to adjust for should be clearly described and withdrawals from each arm of the trial should be detailed. ITT is the preferred mon method is to partition the ␣ level for the trial by subtracting the ␣ level for the interim analysis from the Exploratory subgroup analyses are commonly per- ␣ level intended for the final analysis. Consequently, formed in trials of FGIDs, although their validity is most investigators use a conservative ␣ level, such as .001, for the interim analysis so that sufficient power is evaluates for differences in treatment effects between reserved for the final analysis. If an interim analysis is complementary subgroups (eg, older and younger sub- preplanned, ␣ sharing can be incorporated when calcu- jects), rather than simply comparing P values for each lating the sample size. Unplanned preliminary analysesshould be avoided; premature presentation of results may subgroup, thereby maintaining statistical power.
affect the further conduct of the trial and can lead to the Secondary analyses used to support an efficacy claim should be reporting of inaccurate observations.
ITT analyses. Harms data should be analyzed by ITT when There are few guidelines for conducting interim anal- possible, but absolute incidence rates and 95% confidence inter- yses to assess the futility of continuing a trial. However, to preserve the credibility of the investigators (a) suchanalyses should be overseen by a Data and Safety Moni- toring Board that is independent from the investigators, The protocol should present and clearly specify (b) the analysis should test for equivalence rather than the assumptions underlying the sample size calculation.
superiority of 1 treatment relative to the other, and (c) These elements include the minimum effect size (differ- liberal equivalence margins for the effect size should be ence in primary outcome between groups) that the trial defined a priori and will likely be wider than those is designed to detect, the ␣ (type I) error level, the statistical power or ␤ (type II) error level, and when Interim analyses are not recommended because they may evaluating continuous outcomes (eg, difference in sever- jeopardize the trial integrity unless there is reason to believe ity scores), the standard deviation of the difference. Re- participation in the trial (either in the active treatment or cent trials have been powered to detect differences as control group) places the patient at risk. small as or Often, a power of80% is used (␤ error or type II error of 20%) and ␣ (type I) error of 5% using a 2-sided test. An allowance for The main result of a trial must be presented dropouts should also be made in determining the appro- according to the predetermined primary outcome mea- priate sample size, but efforts should be made to keep the sure(s). Selecting a primary outcome measure after the dropout rate below 10%–20%. It is inappropriate for an trial is concluded inflates the type I error rate and is investigator to conclude, from an inadequately powered misleading. Unexpected results that were not part of the study that fails to find a statistically significant difference between interventions, that the 2 interventions are exploratory, for testing in future studies. Adherence to study goals is strengthened when an independent advi- A sample size calculation should be routinely performed and should be based on the expected behavior of the primary outcome Changing the primary outcome measure(s) in the analysis phase of a study should not be done; it invalidates the statistical Table 2. Recommendations for Future Research 2. Veldhuyzen van Zanten SJ, Talley NJ, Bytzer P, Klein KB, Whor- well PJ, Zinsmeister AR. Design of treatment trials for functional 1. Examine the periodicity and severity of symptoms in natural gastrointestinal disorders. Gut 1999;45(Suppl 2):II69 –II77.
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