The Challenges of Performing Controlled Trials of Diet Therapies in Gastroenterology

ABSTRACT

Dietary trials methodology in the field of translational gastrointestinal research is fraught with constraints, relating to cost, practicalities of executing dietary trials, and the particulars of manipulating foods that often cannot be overcome. As such, dietary interventions may be unfairly judged as low quality. However, dietary trials are commonly poorly designed, based principally on drug trial methodology, which is often not appropriate in the setting of food, has a very different composition, and is not delivered like pharmaceuticals. This risks accurate interpretation of data and a lack of translatability to clinic. Careful attention should be given to the design of dietary trials to ensure studies remain high quality and clinically relevant. This review summarizes the key factors necessary for consideration when executing a well‐designed dietary trial for gastrointestinal conditions and examples of how they have been used and reported on. Key factors include modeling dietary composition to meet the research question, appraising pre‐exposure diets and their impact on the study, interpretation and potential use of placebo and nocebo effects, and the use of sham diets. Finally, measuring and reporting on blinding and adherence, which is essential, as for all trials methodology.

1. Introduction

Randomized controlled double‐blinded parallel trials are widely regarded as the gold standard of clinical research. Such study designs minimize bias and generate high quality data to establish efficacy or inefficacy of therapeutic interventions. However, this model was based upon evaluation for pharmaceutical therapies, which are comparatively straightforward to standardize, administer, and blind. Diet is more complex. Despite this, dietary therapies should be held to the same evidentiary standard as pharmaceuticals and are often scrutinized for lacking robust methodology. Feeding trials are the gold standard of assessing efficacy and safety of dietary therapies [1, 2] as they allow precise control of dietary intake. However, these studies are often expensive, source‐intensive and impractical to implement at scale or over prolonged durations. Unlike pharmaceuticals, design of trial, dietary composition, baseline diet, exposure placebo and nocebo, sham diets, blinding and adherence are all factors that need extensive consideration. Key methodological consideration for dietary and pharmaceutical trials are summarized in Table 1.

TABLE 1.

Key methodological consideration for dietary and pharmaceutical trials.

Characteristic	Pharmaceutical trial	Diet trial
Route of delivery	Oral or injected	Oral
Administered by	Clinician or patient	Patient
Composition	Isolated substances	Specific nutrient in pill/spiked in food or complex matrices of food
Regimen	Doses at specified intervals	Consumed throughout the whole day
Baseline exposure	Usually absent before exposure	Usually present before exposure
Access	No access to study drugs	Readily accessible
Placebo	Easy to make	Difficult to design – sham or comparison to established therapy often used
Impact of pre‐conceived ideas	Small effect	Big effect with common placebo/nocebo response
Blinding	Easy	More difficult or impossible
Adherence	Fair	Often poor
Cost	Cheap or expensive	Expensive if a high‐quality trial

Barriers for executing high‐quality dietary research should be considered when interpreting trial outcomes, including challenges that may be difficult or impossible to overcome. This narrative review will provide insights to critically examine the methodological strengths, limitations and practical considerations of conducting dietary trials in gastrointestinal disease, with a focus on translating trial findings into meaningful clinical practice.

2. Study Design of Diet Trials

Before discussing specific issues related to the design of trials of dietary interventions, it is important to understand how the quality of evidence from the medical literature is judged. Randomized controlled trials (RCT) are judged using the Cochrane risk of bias tool [3]. This assesses the method used to generate the randomization schedule (e.g., computer generated list, random number table, coin toss, etc.), the method used to conceal treatment allocation (e.g., a central organization that was uninvolved with recruitment allocated treatment, sealed opaque envelopes, etc.), whether blinding was implemented for participants, investigators, and those assessing outcomes, whether there was evidence of incomplete outcomes data (e.g., only data from those adhering to the trial protocol and completing follow‐up were included in the analysis), and whether there was evidence of selective reporting of outcomes (e.g., the trial protocol stated that certain endpoints would be used to assess efficacy, but these were not reported). Trials are then judged as being low, unclear, or high risk of bias across these domains.

Obviously, RCT data are summarized and appraised continually, usually as part of evidence synthesis exercises, such as systematic reviews and meta‐analyses. The quality of meta‐analyses of RCTs is assessed and categorized using Grading of Recommendations, Assessment, Development, and Evaluation (GRADE) criteria [4, 5], which are discussed in more detail in an accompanying article [6]. Any meta‐analysis of RCT evidence starts as high quality but can be downgraded based on factors including high or unclear risk of bias of individual RCTs, due to poor reporting of sequence generation or allocation concealment, a lack of blinding, inconsistency (or heterogeneity) between results of individual RCTs, indirectness of the population, the intervention, the comparator, or the outcomes, imprecision within the meta‐analysis, due to small numbers of patients and wide confidence intervals around summary estimates, or evidence of publication bias.

As an example, in a meta‐analysis of RCTs of linaclotide, a secretagogue drug, in irritable bowel syndrome with constipation (IBS‐C), all five trials were at low risk of bias, heterogeneity between trial results was minimal, endpoints were as recommended by the Food and Drug Administration (FDA), and the included trials included more than 3000 patients, with narrow confidence intervals around the summary estimate [7]. Although there were too few RCTs to assess for evidence of publication bias, quality of the evidence for efficacy of linaclotide in IBS‐C would be high, according to GRADE criteria. In contrast, in a recent network meta‐analysis of dietary interventions in IBS, quality of the evidence for almost all direct and indirect comparisons across the network were rated as either low or very low quality [8].

However, there are inherent challenges in the design of non‐drug trials in IBS and other disorders of gut‐brain interaction (DGBI). These problems were highlighted in a Rome Foundation working team report that made recommendations related to the design of trials of brain‐gut behavioral therapies in IBS [9]. These problems apply equally to RCTs of dietary interventions in IBS and mean that such trials will always be judged as being of low quality by GRADE criteria. Issues in non‐drug trials include difficulties with blinding and the choice of a control or comparator intervention, particularly a credible “placebo.” Although the working team report made recommendations as to how these problems could be addressed, no one approach to this was advised, and many of the suggestions made were aspirational and are not reflected in the clinical trial literature, to date. Solutions to some of these, such as blinding and selecting a comparator intervention, will be discussed below, but there are other issues related to the design and reporting of dietary intervention trials, and which impact on how their quality is rated, that are relatively easily remedied.

First, it is important that dietary intervention trial investigators get the basics right, in terms of the reporting of trial methodology. This is the rationale for the CONSORT statement, which should form the basis of the reporting of any RCT [10]. In the aforementioned network meta‐analysis of dietary interventions in IBS [8], even if issues related to difficulties in blinding trial participants are ignored, several of the RCTs did not report the specifics of how treatment allocation was concealed.

Second, attention is needed to issues related to incomplete outcomes data. The randomization process is compromised if patients do not take their allocated treatment. Therefore, patients should be analyzed according to the treatment arm to which they were assigned originally. Options for dealing with missing data from patients who drop out of the trial early include the assumption that they are non‐responders to treatment, carrying forward the last observation made about treatment response, or imputation of the endpoint for treatment response. The best choice of accounting for missing data depends on the type of data collected and the frequency of measures. For example, carrying forward the last observation is often implemented for missing continuous IBS symptom scores that are measured at several times points throughout the trial, whereas the assumption that missing data represent non‐responders to treatment may be taken for a categorial global symptom question to assess adequate relief of symptoms, measured only before and after treatment.

Third, selective reporting of outcomes should be avoided. A statistical analysis plan, including all planned endpoints, should be written and agreed prior to trial commencement. When the trial is completed and data have been analyzed, the endpoints used to judge response to treatment should be described in the methodology section of the final article reporting the results of the RCT. These endpoints should be entirely consistent with the agreed trial protocol, and the results of all these endpoints should be reported in the final article. The trial protocol should, ideally, be published and available. If not, it should be provided as supporting information when the final article reporting the results of the trial is submitted for consideration for publication.

Finally, although endpoints such as a 50‐point decrease in the IBS severity scoring system are widely accepted, they are not stringent and lead to high placebo response rates. Their use is acceptable as a secondary endpoint, but dietary intervention trials should apply, or approximate, FDA‐recommended endpoints to avoid accusations that their efficacy is being judged by different criteria to drugs. There are accepted FDA‐recommended endpoints for treatment trials in IBS‐C and IBS‐D [11], and European Medicines Agency (EMA)‐recommended endpoints for treatment trials in IBS‐C, IBS‐D, and IBS‐M [12]. Recent examples of dietary intervention trials that have used such approaches, including a trial of a diet low in fermentable oligo, di, and monosaccharides and polyols (FODMAP) versus a FODMAP‐simple diet and an RCT of an IgG‐based elimination diet versus a sham dietary intervention in IBS [13, 14]. Although these can be harder to apply in pragmatic trials recruiting mixed populations of patients with IBS, adequate relief of symptoms is an acceptable endpoint in this situation [15], even in drug trials [16].

When designing a dietary trial for evaluation in a gastrointestinal condition, key factors unique to examining the impact of diet that should be considered include the dietary composition of the intervention, consideration of habitual diet when entering into the trial, placebo and nocebo effects, choice of a comparator diet, such as a sham dietary intervention, adequate blinding, and adherence to the diet. Crosschecking the quality of trials using CONSORT guidelines is recommended for ensuring broader essential features for study design in addition to diet‐specific aspects previously published [1]. Key considerations are described below and illustrated in Figure 1.

FIGURE 1.

Schematic of key factors needing consideration in study design of dietary trials applied for gastrointestinal disease.

2.1. Dietary Composition

There are three main considerations when defining diet composition in interventional trials—representation of normal dietary exposure, choice of comparator diet, and dietary collinearity. Unlike nutraceutical studies, which often administer supraphysiological doses of isolated nutrients in purified form, diet therapies typically involve changes in food choice. Pure supplements, such as n‐3 fatty acid capsules, do not reflect usual dietary exposure, where the n‐3 fatty acids are consumed within the complex food matrix of fish. Then, more broadly, how that fish is eaten in the context of a whole diet, where other foods exert additive, synergistic, or inhibitory effects. This distinction is particularly relevant when progressing from proof‐of‐concept studies to the translational trials based on real food.

The relevance and biological plausibility of the food component or diet under investigation must also be carefully considered. This is well illustrated by the translation of the proof‐of‐concept mouse study implicating the emulsifier polysorbate 80 in the pathogenesis of Crohn's disease [17]. When this finding was translated into human dietary trials, however, the experimental exposure in mice was almost three million‐fold higher than the estimated intake achieved in a high emulsifier diet, based from real food [18]. Such discrepancies highlight the challenges of extrapolating mechanistic findings to clinically meaningful dietary interventions.

The choice of dietary comparator has historically been poorly considered in dietary trials. Comparator diets must be sufficiently distinct from the intervention to enable detection of meaningful differences in outcomes, while remaining controlled and credible. Frequently, healthy eating guidelines are used as a comparator, however, this approach is only appropriate when the intervention differs substantially in composition. For example, an “anti‐inflammatory diet” that aimed to increase antioxidants, fiber, probiotics, n‐3 fatty acids while decreasing red and processed meat and added sugar, was compared to Canada's healthy eating guidelines, resulting in two diets that were similar [19]. Unsurprisingly, no differences were observed in relapse rates among individuals with quiescent ulcerative colitis [19]. In contrast, a head‐to‐head trial comparing a Mediterranean diet (high in plant‐based food, olive oil and low in red and total meat) with a specific carbohydrate diet (that restricts many plant‐based foods, such as grains, starchy vegetables and legumes) examined two contrasting diets [20].

Finally, dietary collinearity is a major challenge and often difficult, if not impossible, to overcome. In community settings, a well‐recognized example is self‐reported non‐coeliac gluten sensitivity, where gluten is assumed to be the symptom trigger. However, multiple trials have demonstrated that symptoms are more accurately attributed to the carbohydrate (FODMAP) content of the wheat rather than the gluten itself [21, 22]. Dietary collinearity is also common when evaluating whole diet interventions, making it challenging to identify the specific dietary components responsible for observed effects. Indeed, this issue was evident in a study assessing dietary influences on ulcerative colitis relapse, where diets designed to modify fat intake also differed in protein, carbohydrate, fiber, sugar, and multiple micronutrients, complicating interpretation of the role of fat alone [23]. Even in tightly controlled feeding studies, precise control of all dietary variables can be difficult to achieve, as demonstrated in comparisons of low and high emulsifier diets that also differed in their proportion of ultra‐processed foods [18].

2.2. Baseline Diet Exposure

Preconceived ideas about diet and the resulting baseline diet exposure can strongly influence studies outcomes. Such beliefs may drive placebo and nocebo responses, as seen in individuals with self‐reported non‐coeliac gluten sensitivity [21, 22]. Beyond perceptual effects, baseline diets may also have a physiological impact that modifies responses to the diet intervention. For example, self‐imposed dietary restriction prior to trial enrolment may lead to alteration of gut microbiota, which could exaggerate or attenuate the observed effects of the intervention.

2.3. Placebo and Nocebo

Placebo‐ and nocebo‐ effects are common in medicine and need to be considered in the context of dietary interventions. They shape how patients feel, how symptoms change, and how therapies appear to work, both in practice and in research. A placebo is an inert intervention that has no specific therapeutic effect for the treated condition. The term also describes the benefit that arises from receiving treatment, rather than from defined pharmacologic effects of a treatment. Placebo responses are clinical improvements that occur after placebo administration or within a treatment context lacking active components, driven by patient expectations, conditioning, and the psychosocial environment or spontaneous improvements [24].

In contrast, a nocebo effect is the onset or worsening of symptoms or adverse events driven by negative expectations, contextual cues, or prior treatment experiences, not by a pharmacologic action. Nocebo responses can stem from information about side effects, prior negative experiences, or anticipatory anxiety [25] and nocebo responses can be important for dietary interventions when exclusion and re‐exposure diets are tested [21].

Both placebo and nocebo responses can accompany active therapies and influence outcomes. Understanding these responses requires recognizing multiple mechanisms, some independent of the active drug. The intensity of symptoms in many diseases or disorders, such as DGBI, changes over time with symptoms waxing and waning, and even objective markers (such as endoscopically assessed mucosal lesions in patients with inflammatory bowel disease) can vary without therapy [26].

The gain over placebo is widely considered the most important measure of an intervention's effectiveness. This interpretation of the active—placebo difference is based upon the assumption that whatever beneficial process operates during placebo therapy operates equally during active therapy. This would not be true if the active therapy acts directly and causally on the underlying source of symptoms and subsequently annulling for example, the effect of natural history. While this possibility is difficult to evaluate, the assumption that the difference between active and placebo is the only response attributable to the active therapy is fundamentally important, as it limits our estimates of therapeutic efficacy and, in doing so, underscores the importance of understanding the placebo response. Indeed, a strong placebo is frequently observed in conditions with pain as the primary target for interventions [27], which is also relevant for many DGBI such as functional dyspepsia [28]. This may also imply that placebo (and nocebo) effects are mediated by specific neurobiological mechanisms, including endogenous opioids, descending pain modulation, and placebo‐related autonomic changes. This effect might be compounded by conditioned responses, such as exposure to a clinic setting associated with previous experiences and subsequent expectations or the appearance of medications [29].

In routine clinical practice, nocebo and placebo operate together. Distinguishing their contributions to clinical outcomes is important for interpreting clinical studies. While regulators and researchers need to account for these effects, clinicians can leverage placebo effects by achieving “sufficient” improvement through the combined effects of the “dietary or pharmacologic intervention” and placebo. At the same time, it is important to minimize nocebo effects by for example, addressing fears and concerns in relation to adverse outcomes of therapies by appropriate patient information and information.

2.4. Sham Diets

In high‐quality, randomized controlled dietary advice trials, a sham diet is used as the placebo. A sham diet mimics the therapeutic appearance and complexity of an experimental diet while maintaining a typical daily nutrient intake comparable to that of the general population [30]. Delivery of sham dietary advice is a clinically applicable, cost‐effective dietary intervention strategy compared to a feeding study where food is provided, however, risks dietary collinearity even with comprehensive dietary counselling [1]. Unlike a pharmaceutical placebo, sham diets are notoriously complex to design due to the intricate matrices of food and strategies required to minimize the influence of preconceived dietary beliefs on therapeutic outcomes [30]. Poorly planned sham diets risk successful blinding and subsequent identification of the true intervention diet. This is becoming more complex for some diet therapy trials where dietary advice has become an accepted and accessible diet therapy (e.g., low FODMAP diet). Furthermore, without a detailed description of the sham dietary prescription including accompanying scientific rationale for diet construction, sham diets are unable to be replicated in future trials as observed in historical IBD diet trials which limits analysis of trial data [31].

Until recently guidance on how to develop sham diets has been limited, with some notable exceptions [30, 32]. A small number of successful sham diet trials for gastrointestinal diseases and disorders have been conducted [33, 34, 35]. Learnings from these and other interventional diet trials have informed a six‐step approach to designing a placebo‐control sham diet, intending to overcome common pitfalls of diet trials. These include acceptance and tolerability of, and adherence to, the prescribed diet, and rigorously evaluating for dietary components in sham diet design, which are identified as inert or controlled for their effects within the intraluminal environment. A suggested six‐step approach to designing a sham diet [30] is detailed in Table 2.

TABLE 2.

Six‐step approach to designing a sham diet.

Step	Process stage	Description
1	Diet characterization	Profile the experimental diet
2	Comparator design	Profile the sham diet
3	Component selection	Identify suitable food and food components to include and/or exclude
4	Delivery development	Develop a sham dietary delivery to mirror the experimental diet
5	Meal plan design	Develop a sham set meal plan to mirror the experimental diet
6	Education strategy	Develop sham education materials and accompanying dietary advice to mirror experimental diet education strategy

To rigorously evaluate therapeutic appearance and success of blinding the sham diet, piloting prior to use in the intended larger trial is recommended [30]. By doing so, a sham diet can be further refined to ensure its integrity as a placebo‐control. This is a critical step to which there are scarce data published, with many diet advice trials opting for active diet comparators (e.g., Crohn's disease exclusion diet advice vs. exclusive enteral nutrition) [36] or re‐supplementation dietary advice trials (e.g., gluten re‐supplementation in coeliac disease) [37].

2.5. Blinding

Blinding of entire diets for both patients and researchers is inherently challenging if not impossible. The ability to achieve successful blinding will highly depend on the choice of placebo or comparator. This is particularly so where the form of dietary manipulation is well‐known. For example, in a high vs. low fiber dietary intervention, both participants and researchers are likely to recognize foods that are high or low in fiber. One way of overcoming this issue, as demonstrated in a recent dietary trial, was to supply the same background diet across different interventions, varying only selected foods in their fiber content [38]. The success of blinding was therefore achieved in this trial, with 2 of 3 participants incorrectly guessing their treatment allocation. Furthermore, the availability of dietary information on the internet can also compromise the integrity of blinding. Concealing dietary terms from participants may aid this risk of internet unblinding, as performed in a dietary trial of a low vs. high FODMAP diet whereby the term FODMAPs were not mentioned in the dietary education nor was the purpose of the study [39]. Whilst no formal evaluation of blinding was performed, a high proportion of patients were not able to distinguish their allocated diet, suggesting that blinding was preserved.

An increasing number of dietary feeding trials are reporting the possibility of achieving double blind with good success [40, 41, 42, 43]. In these studies, the provision of food or meals was similar in appearance and packaging for both the intervention and control diets and meal plans appeared the same. However, what must be considered is the cost‐ and resource‐intensive nature of double‐blinded feeding trials, often involving a large research team preparing the study diet. On the other hand, in dietary advice trials, it is not possible to blind the dietitian administering the advice. Ensuring data analysis is conducted by someone who is blinded to diet allocation is recommended in these settings.

For all dietary intervention trials, the success of blinding should be assessed and reported in order to assess intervention fidelity and subsequently, the effect of adequate blinding on study findings.

2.6. Adherence

Adherence is central to the treatment effect of a diet therapy. Intent and efficacy of a diet therapy are uninterpretable without measuring adherence. The basis of a diet or food component(s) having therapeutic effects relies on the assumption that the diet is followed. Therefore, dietary adherence is a critical part of diet trial design and reporting of outcomes [1]. Unfortunately, reporting on adherence to dietary trials is uncommon. Indeed, in a review of 40 studies evaluating food‐based dietary interventions for inflammatory bowel disease, < 60% of studies reported on subjective or objective markers of adherence to therapeutic diets [31]. In addition to supporting cause‐and‐effect for a diet, evaluating adherence also measures other important outcomes unique to diet trials, like tolerability, acceptability, nutritional adequacy, and food‐related quality of life.

Measuring adherence to a dietary therapy becomes increasingly more difficult with multiple altered components. For example, measuring adherence to exclusive enteral nutrition, a liquid‐only diet replacing food, requires only the assessment of whether food has been eaten. Conversely, adherence to a Mediterranean diet requires the assessment of foods that have been consumed and limited, in addition to their volume and frequency. If the diet is instructed rather than provided in a feeding trial, there may be challenges with participants' meal preparation, food knowledge, and basic cooking skills [44].

Another key issue with measuring adherence is a lack of validated objective biomarkers. Unlike measuring drug levels, which is often conducted in pharmaceutical trials, dietary adherence often relies on subjective measures, such as dietary recall or food diaries, which are poor surrogates with high probability of reporting bias. Biomarkers of adherence are being developed (e.g., production of fecal hydrogen sulphide as a measure of adherence to high fiber, lower animal protein diet or volatile organic compounds as a predicator of response to low FODMAP diet) [31, 45]. One of the predicaments of evaluating adherence to diet therapies relates to appropriateness and validation of adherence tools. Each diet strategy is likely to require its own adherence tool (e.g., biomarker or adherence questionnaire), unlikely to be interchangeable between different therapeutic diets. For example, there are many questionnaire‐based adherence tools that are used for a Mediterranean diet but not appropriate for assessment of other diets or variations to a Mediterranean‐style diet [46, 47]. The method of measuring adherence must be appropriate and reliable—best achieved with a combination of subjective and objectives measures. Trained personal such as a dietitian are critical to providing support and monitoring adherence and should be involved in trial design, implementation of diet and reporting of outcomes to achieve the highest possible methodological rigor.

3. Conclusions

Dietary trials to treat gastroenterological conditions are being conducted more frequently. Thus, careful consideration of their design and the interpretation of data is required (Figure 1). The key factors to consider in study design include the study population and the altered dietary components of the trial. Firstly, attention must be given to the patients undertaking the study, including the composition of their habitual diets and whether they have preconceived ideas about diet, which may predispose them to placebo or nocebo responses. Secondly, the interventional diet and comparator need thorough design, particularly if a sham diet is to be used. Thirdly, there should be an assessment of adequate blinding and adherence. Only with such regard will dietary studies be held to a high standard for evaluation of efficacy and value for translation into clinical practice.

Funding

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Conflicts of Interest

The authors declare no conflicts of interest.

Data Availability Statement

Data sharing not applicable to this article as no datasets were generated or analysed during the current study.