Bile acids for metabolic dysfunction‐associated steatotic liver disease in adults

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

To evaluate the benefits and harms of oral bile acid‐based therapies versus no intervention or placebo, or versus a different bile acid‐based therapy, at any dose or regimen, in adults diagnosed with metabolic dysfunction‐associated steatotic liver disease (MASLD).

Background

Description of the condition

Metabolic dysfunction‐associated steatotic liver disease (MASLD), previously known as non‐alcoholic fatty liver disease (NAFLD), is the most common chronic liver disorder in the world, with a global prevalence of up to 30% of the world population [1, 2, 3]. MASLD has been steadily increasing in prevalence, along with obesity and type 2 diabetes mellitus [4]. Amongst people with type 2 diabetes mellitus, the global prevalence of MASLD was 55.5% (95% confidence interval (CI) 47.3% to 63.7%) [5]. Obesity, physical inactivity, age, sex, ethnicity, or dyslipidaemia are all factors that influence the prevalence of the MASLD [6, 7, 8, 9, 10, 11]. MASLD is associated with a wide spectrum of liver disorders, from simple fatty liver (i.e. steatosis, with accumulation of fat droplets in more than 5% of the liver cells, without cell injury) to metabolic dysfunction‐associated steatohepatitis, formerly known as non‐alcoholic steatohepatitis, with inflammatory hepatocyte injury (ballooning) with or without fibrosis, and increasing fibrosis leading to cirrhosis (end‐stage liver disease) [3, 12, 13]. Hepatocellular carcinoma can develop in genetically predisposed people with MASLD [14]. MASLD is the second cause of liver transplantation in the USA [15, 16]. It can develop 'de novo' even after liver transplantation [17]. People with MASLD also frequently have cardiovascular diseases, primarily affecting the heart or the brain [18]. Cardiovascular diseases are the leading cause of mortality in the MASLD population [19].

The definition of MASLD is based on the evidence of hepatic steatosis in the presence of at least one of the following five cardiometabolic criteria for adults [20, 21].

• Overweight/obesity with body mass index (BMI) of 25 kg/m² or greater (23 kg/m² or greater in Asian people) or waist circumference of 94 cm or greater in Caucasian men and 80 cm or greater in Caucasian women (or ethnicity‐adjusted equivalent)

• Fasting glucose levels of 5.6 mmol/L or greater (100 mg/dL or greater) or two‐hour postload glucose levels of 7.8 mmol/L or greater (140 mg/dL or greater) or glycated haemoglobin (HbA1c) of 5.7% or greater (39 mmol/L or greater) or type 2 diabetes or treatment for type 2 diabetes

• Blood pressure of 130 mmHg/85 mmHg or greater (systolic/diastolic) or specific antihypertensive drug treatment

• Plasma triglycerides of 150 mg/dL or greater (1.70 mmol/L or greater) or specific lipid‐lowering treatment

• Plasma high‐density lipoprotein‐cholesterol less than 40 mg/dL (less than 1.0 mmol/L) for men and less than 50 mg/dL (less than 1.3 mmol/L) for women or specific lipid‐lowering treatment.

The pathogenesis of MASLD is unclear. The last 'multiple hit' hypothesis explains the mechanistic stages of liver injury [22]. It considers any interruption in the balance of the gut microbiome, insulin resistance, obesity, oxidative stress, and the disharmony of inflammatory cytokines, as well as epigenetic factors acting together, to predict progression and the development of MASLD in genetically predisposed individuals [22, 23]. There is no pathogenetic explanation for the clinical and morphological heterogeneity in MASLD [24].

The diagnosis of MASLD is often made on abnormal imaging of the liver or elevated serum liver enzymes, and it involves the exclusion of other causes of liver injury, such as excessive alcohol consumption, viruses, autoimmune liver disease, genetic disorders, starvation, and the use of hepatotoxic drugs [25, 26, 27]. Covert or hidden alcohol consumption continues to be a commonly missed problem in the diagnostic workup of people with suspected MASLD, and repeated interviews assisted by questionnaires to reveal covert or hidden alcohol problems are often needed. Imaging techniques, such as ultrasound screening or transient elastography, proton magnetic resonance spectroscopy, and quantitative fat or water‐selective magnetic resonance imaging, are used to establish the presence of hepatic steatosis in MASLD, assess liver fibrosis, or quantify liver fat [28, 29], in addition to liver biopsy [13, 30].

Description of the intervention and how it might work

Bile acids are naturally occurring molecules synthesised from cholesterol and conjugated to amino acids in the liver. These are called primary bile acids. Intestinal bacteria alter the primary bile acids into secondary bile acids. Then they return to the liver via the portal circulation.

Bile acids are stored in the gallbladder. They are essential for the digestion and absorption of dietary fats and fat‐soluble vitamins, and play a role in cholesterol homeostasis and gut microbiota composition. In addition to these physiological functions, bile acids act as signalling molecules that influence metabolic pathways, including lipid and glucose metabolism, through activation of nuclear and membrane receptors [31].

The spectrum of bile acids includes cholic acid, chenodeoxycholic acid, deoxycholic acid, lithocholic acid, ursodeoxycholic acid, norursodeoxycholic, obeticholic, taurocholic, and lithocholic acids.

Amongst the bile acids, oral administration of ursodeoxycholic acid and obeticholic acid is used as therapeutic agents in MASLD. Both acids are under investigation for their anti‐inflammatory and antifibrotic properties to reduce inflammation and fibrosis in liver diseases [32, 33]. Bile acids may reduce hepatic lipogenesis, steatosis, and insulin resistance [34, 35]. Oral administration of bile acid derivatives can modulate both the composition of the endogenous bile acid pool and the gut microbiota, potentially offering metabolic benefits in MASLD [36, 37, 38].

Beyond their digestive roles, bile acids interact with several receptors — such as the farnesoid X receptor, pregnane X receptor, vitamin D receptor, and G‐protein‐coupled bile acid receptor — to regulate energy homeostasis, detoxification, and immune responses [31, 34, 39]. Farnesoid X receptor activation, for example, induces fibroblast growth factor‐19, which downregulates bile acid synthesis by suppressing CYP7A1 and modulates cholesterol and glucose metabolism [40].

People with MASLD exhibit dysregulation in bile acid metabolism, including increased faecal bile acid excretion, elevated serum levels of primary bile acids, and impaired feedback regulation. This dysregulation may contribute to hepatic cholesterol accumulation and disease progression [40].

Lifestyle modification, a healthy diet, and controlling comorbidities such as type 2 diabetes mellitus are the usual interventions for MASLD [41, 42, 43]. A supplementary intervention for people with MASLD includes the oral bile acids, ursodeoxycholic acid and obeticholic acid [44]. The European Association for the Study of the Liver – European Association for the Study of Diabetes – European Association for the Study of Obesity (EASL–EASD–EASO) Clinical Practice Guidelines provide dose recommendations for two of the bile acids (i.e. ursodeoxycholic acid and obeticholic acid). The recommendations of the best doses and regimens for treating people with MASLD were selected using consensus, as evidence from systematic reviews with meta‐analyses of randomised clinical trials is lacking [45]. There are no recommendations for the best doses and regimens of the remaining bile acid derivatives in clinical settings.

Our knowledge of adverse events is also sparse. In one 2023 market report overview on ursodeoxycholic acid, under "Side effects of using ursodeoxycholic acid to bring down market growth," it is written that "using this acid continually for a very long time can still cause some side effects [meaning adverse effects] to the human body …" The report also states that "Ursodeoxycholic acid can cause certain problems which involve bloody or cloudy urine, faster heartbeat, severe nausea, stomach pain, skin rashes, body itchiness, frequent urge to urinate, severe bladder pain, and difficulty in urination" [46]. Obeticholic acid, also known as Ocaliva, is associated with well‐recognised adverse effects. The most common adverse events are pruritus, fatigue, abdominal pain and discomfort, arthralgia, sore throat, dizziness, and constipation [47]. In addition, although less frequent, there have been reports of hepatotoxicity, including people experiencing serious liver‐related adverse events, particularly in those with advanced cirrhosis [48].

Why it is important to do this review

Leoni and colleagues have critically reviewed and assessed five international guidelines for similarities and discrepancies in the diagnosis and treatment of MASLD [30]. They found that the five clinical guidelines, except for lifestyle modification treatments, are discordant in their recommendations on the management of people with MASLD. Evidence for possibly helpful medicines is either insufficient or lacking [30, 42, 49, 50]. A consensus report from 2022 also concluded that there is no high‐quality evidence for liver‐specific management in NAFLD (now known as MASLD) [51].

One Cochrane review by Orlando and colleagues published in 2007 included four clinical trials with 279 participants randomised to ursodeoxycholic acid versus placebo (three trials) with or without a low‐calorie diet, or versus vitamin C and E. The review found insufficient data to support or refute the use of bile acids in people with MASLD [52]. Though we identified two meta‐analyses on ursodeoxycholic acid and obeticholic acid in people with MASLD, the included trials used non‐invasive markers to assess progression of fibrosis, and the majority of the assessed outcomes were unvalidated surrogate outcomes [53, 54]. Some randomised clinical trials of norursodeoxycholic acid and obeticholic acid in people with MASLD showed beneficial results [55, 56, 57].

Given the increasing prevalence of MASLD, the growing administration of bile acids and their derivatives, with no proven effects, the long‐term risks associated with comorbidities, and the current guideline recommendations on bile acids in people with MASLD, there is a need to conduct a systematic review with meta‐analyses of randomised clinical trials, aiming to evaluate the available evidence on the use of bile acids versus no intervention, placebo, or another bile acid in people with MASLD.

Objectives

To evaluate the benefits and harms of oral bile acid‐based therapies versus no intervention or placebo, or versus a different bile acid‐based therapy, at any dose or regimen, in adults diagnosed with metabolic dysfunction‐associated steatotic liver disease (MASLD).

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised clinical trials with a parallel‐group design, irrespective of language, format, year, status of publication, and the outcomes measured or reported.

Though unlikely, if we identify cluster‐randomised trials or trials with a cross‐over design, we will include them. In cluster‐randomised trials, groups of individuals are randomised to different interventions [58]. In trials with a cross‐over design, each participant is allocated to a sequence of interventions [58].

We will exclude quasi‐randomised studies as the method of allocation of participants to the study groups is not truly random (e.g. based on date of birth, data entry) and any other observational studies.

Types of participants

We will include adults aged 18 years or older, any sex, gender, race, ethnicity, and setting, diagnosed with MASLD at any stage (i.e. MASLD in people with or without liver fibrosis, or cirrhosis with compensated stage). We will accept any definitions used by the trial authors when describing the diagnosed trial participants.

If we identify a trial that includes a subset of participants with diseases other than MASLD (i.e. the arbitrary greater than 10%), and we cannot separate their data from the data of interest for our review, we will contact trial authors to request the data. If we cannot obtain the data or if the trial authors do not respond, then we will exclude the trial. If the subset is 10% or less, we will include the trial, irrespective of response, and we will perform a sensitivity analysis.

We will exclude trials with participants having chronic liver disease other than MASLD, such as alcoholic liver disease, hepatitis B, or hepatitis C. We will record if and how people with alcohol problems were excluded in the individual trials. We will also register whether alcohol consumption was monitored during the trial.

Types of interventions

Experimental intervention

• Any bile acid drug administered at any dose, treatment duration, or regimen

Control interventions

• No drug intervention or placebo

• A different experimental bile acid drug administered at any dose or regimen

We will allow co‐interventions if administered equally to the trial intervention groups.

Outcome measures

If data are provided at more than one time point (i.e. by the end of treatment, during post‐treatment, and at the longest follow‐up), we will record and analyse the data of the three time points. Our primary analyses for conclusions will consist of outcome data at the longest follow‐up. We will use the outcome data at the remaining two time points for secondary analyses.

We will also include trials that do not report results of outcomes they might have measured or do not provide usable data.

We have selected our critical and important outcomes to align with clinically meaningful outcomes commonly used in regulatory trials of treatments for liver disease, including all‐cause mortality, liver‐related mortality, serious adverse events, liver‐related morbidity, and health‐related quality of life measured by validated tools.

Critical outcomes

• All‐cause mortality.

• Liver‐related mortality.

• Proportion of people with one or more serious adverse events. We will use the definitions employed by the trial authors for serious adverse events as well as the definition in the International Conference on Harmonisation (ICH) Guidelines for Good Clinical Practice [59] (i.e. any untoward medical occurrence that results in death, is life‐threatening, requires hospitalisation or prolongation of existing hospitalisation, results in persistent or significant disability or incapacity, or is a congenital anomaly or birth defect). We will consider any other adverse event as non‐serious (see Important outcomes). As the 'serious adverse events' outcome is a composite outcome, we will also perform secondary analyses of the individual components of the composite outcome.

Important outcomes

• Liver‐related morbidity (a composite of gastrointestinal bleeding, ascites, hepatic encephalopathy, hepatorenal syndrome, jaundice, hepatocellular carcinoma, or need for liver transplantation).

• Health‐related quality of life. We will consider trial data only if trialists have used validated tools to measure health‐related quality of life, such as World Health Organization Quality of Life (WHOQOL), EuroQoL Group Quality of Life Questionnaire based on 5 dimensions (EQ‐5D), 36‐item Short Form Health Survey (SF‐36). We will use these tools in the order provided.

• Proportion of people with one or more adverse events considered non‐serious (see Critical outcomes).

• Proportion of people with no change in fibrosis or worsening of fibrosis.

• Proportion of people with no resolution of metabolic dysfunction‐associated steatohepatitis.

Search methods for identification of studies

To minimise bias in our search results, we will follow the guidance in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Interventions [60] and in PRISMA‐S [61] on planning and describing the search process for the review. The Cochrane Hepato‐Biliary Group Information Specialist will develop the final search strategies and perform the electronic searches. We will not impose any restrictions on the language of publication, date, or status.

Electronic searches

We will search the Cochrane Hepato‐Biliary Group Controlled Trials Register via the Cochrane Register of Studies Web, Cochrane Central Register of Controlled Trials in the Cochrane Library, MEDLINE ALL Ovid, Embase Ovid, LILACS (Latin American and Caribbean Health Science Information database; VHL Regional Portal), Science Citation Index Expanded, and Conference Proceedings Citation Index – Science. We will search the latter two simultaneously through the Web of Science.

We will use the Cochrane Highly Sensitive Search Strategies for identifying randomised trials in MEDLINE and Embase, modified to include relevant search terms for identifying retraction statements and errata, as recommended in Chapter 4 of the Cochrane Handbook for Systematic Reviews of Interventions [60, 62].

Supplementary material 1 shows the preliminary search strategies with the expected date range of the searches. We will provide the actual date of the electronic searches at the review stage.

Searching other resources

We will search online trial registries such as the US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (https://clinicaltrials.gov), European Medicines Agency (https://euclinicaltrials.eu/search-for-clinical-trials/), World Health Organization International Clinical Trials Registry Platform (https://trialsearch.who.int), the US Food and Drug Administration (https://www.fda.gov), eLibrary (https://www.elibrary.ru), VINITI (https://www.viniti.ru/database), Russian Medicine (https://medjrf.com/0869-2106), and pharmaceutical company sources for ongoing or unpublished trials. We will attempt to search Chinese databases through the Chinese Cochrane Centre.

We will search for grey literature such as meeting abstracts and internal reports in Europe OpenGrey (https://www.opengrey.eu), and Google Scholar (https://scholar.google.com).

We will use the PubMed/MEDLINE 'similar articles search' tool on all included trials. We will manually check citations and reference lists of the included trials, and of any relevant systematic reviews identified.

We will search for and examine any relevant retraction statements through the Retraction Watch Database (https://retractionwatch.com/retraction-watch-database-user-guide/), and errata for information, as errata can reveal important limitations or even fatal flaws in studies [62].

We will screen reference lists of included trials, and may contact the trial authors, to identify further published or unpublished trials of potential interest for our review.

We will provide the search terms used for the above‐listed resources and the dates of search at the review stage.

We will use the relevant sections of the PRISMA‐S checklist for our review to ensure that we have reported and documented our searches as advised (PRISMA‐S Checklist [61]).

Data collection and analysis

We will follow the guidelines provided in the Cochrane Handbook for Systematic Reviews of Interventions [63]. We will perform our main analyses using Review Manager [64]. We will assess imprecision with Trial Sequential Analysis and compare the assessment with our assessment with GRADE in a sensitivity analysis [65, 66, 67, 68].

Selection of studies

We will use Covidence software for screening of search results and trial selection [69]. One review author (REA) will upload the list of all candidate studies in Covidence and will remove duplicates of the same study. Three review authors (REA, DN, and CSP) will independently screen titles and abstracts to identify the studies of possible interest. We will retrieve the full‐text publications of potentially eligible studies, and the same three review authors will assess the trials based on the inclusion and exclusion criteria described in this protocol. The same three review authors will screen reference lists of trial reports to identify further trials of potential interest for our review.

We will include conference abstracts, unpublished trials, and grey literature reports if we can use the data for analysis. We will also include trials that do not assess or report data on outcomes of interest for our review, even if trial investigators, after personal communication, do not send us the requested data. We will resolve any disagreements by discussion or by involving any of the three remaining review authors (OB, PA, or CG), for arbitration. We will list the studies excluded during the full‐test assessment in 'Excluded studies'. We will record the selection process in sufficient detail to complete a PRISMA 2020 flow diagram (for new systematic reviews, which includes searches of databases, registers, and other sources) [70, 71].

To screen non‐English‐language publications, and if we do not have command of a certain language, we will use Google Translate to assist with eligibility assessment (https://translate.google.com). If needed, we will look for translators with the help of the Cochrane Hepato‐Biliary Group Editorial Team office to assist with eligibility assessment and data extraction.

Data extraction and management

We will use Covidence software for data extraction [69]. Three review authors (REA, DN, and CSP) will independently extract data from the trials fulfilling the protocol inclusion criteria, using a data extraction form, piloted on a few trials. If a trial is reported in more than one publication, we will extract data from each report separately and then combine the information across the multiple data collection forms ensuring there is no duplication of data. We will resolve disagreements by discussion or with any of the remaining three review authors (OB, AC, or CG).

For our review, we will record the information below.

• Publication data (i.e. title, format of publication, year (range of years) of conductance of the trial and language of publication, place and country of the recruited participants, setting, authors; contact author email for correspondence).

• Study design.

• Funding.

• Registered trial protocol.

• Setting: inclusion and exclusion criteria; methods of randomisation, including allocation sequence and concealment, to identify quasi‐randomised studies.

• Sample size calculation performed and reached, or not.

• Population data (i.e. age, sex, gender, race, ethnicity, history of the disease, ethnicity, and MASLD stage).

• Intervention data (type of intervention in the experimental and control group(s), dose, frequency, duration of intervention, and concurrent medications used).

• Outcomes.

• Dropouts and reasons for them.

• Length of follow‐up; other time points with follow‐up data.

• Types of data analyses (i.e. intention‐to‐treat, modified intention‐to‐treat, per‐protocol).

• Number of participants randomised.

• Number of participants included in the analysis.

• Number of participants with events for binary outcomes, mean and standard deviation (SD) for continuous outcomes, number of events and the mean follow‐up period for count outcomes, and number of participants with events and the mean follow‐up period for time‐to‐event outcomes.

• Any valid information that can be extracted from ongoing trials.

• Any information on withdrawn or retracted trials if such is found.

We will ensure that we have retrieved and collected all available and relevant data for our review from the trial publications and through correspondence with study publication authors. We will enter details of our correspondence with the trial publication authors in the 'Characteristics of included studies' table.

Risk of bias assessment in included studies

Two review authors (REA and CSP) will independently assess the risk of bias for each outcome at the longest follow‐up, using the Cochrane RoB 2 tool (https://www.riskofbias.info/; 72, 73; Critical outcomes; Important outcomes). For the outcome 'health‐related quality of life', we will follow the guidance in Section 8.6 of the Cochrane Handbook for Systematic Reviews of Interventions [72]. We will resolve disagreements by discussion with a third review author (PA, DN, or CG).

We will assess the effect of the assignment on the intervention using the intention‐to‐treat (ITT) principle, which includes all randomised participants, irrespective of the interventions that participants received.

We will assess the following five RoB 2 domains for each outcome in the randomised trials.

• Bias arising from the randomisation process

• Bias due to deviations from intended interventions

• Bias due to missing outcome data

• Bias in the measurement of outcome

• Bias in the selection of the reported result

Each domain contains a series of signalling questions, with the answers (yes, probably yes, no information, probably no, no). Elaborations on these signalling questions can be found in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions [72]. We will determine the risk of bias in each domain (low risk, some concerns, and high risk). We will include text alongside the judgements to provide supporting information for our decisions, including when our risk of bias assessment is due to additional correspondence with trial authors.

Each domain will obtain one of the three levels below.

• Low risk of bias: the trial is at low risk of bias for all domains for this result.

• Some concerns: the trial is judged to raise some concerns in at least one domain for this result, but is not at high risk of bias for any of the remaining domains.

• High risk of bias: the trial is at high risk of bias in at least one domain for this result, or the trial is judged to have some concerns for multiple domains in a way that substantially lowers confidence in the result.

The overall risk‐of‐bias judgement is the same as for an individual domain, such as low risk of bias, some concerns, or high risk of bias. Judging a result to be at a particular level of risk of bias for an individual domain implies that the result has an overall risk of bias at least this severe.

We will summarise the risk of bias in the forest plots and in the text based on ITT.

We will assess the risk of bias of all our Critical outcomes and Important outcomes at the longest follow‐up time point. As risk of bias is one of the five GRADE domains, we will use our risk of bias assessments to assess the certainty of the body of evidence [74]. In our 'Summary of findings' tables, we will present the outcomes below as these outcomes are considered most clinically important.

• All‐cause mortality

• Liver‐related mortality

• Proportion of people with one or more serious adverse events

• Liver‐related morbidity

• Health‐related quality of life

• Proportion of people with one or more adverse events considered non‐serious

In case of cross‐over trials of interest to our review, we will use the standard version of RoB 2 as we will use the data from the first period only [58, 72, 73]. If we identify cluster‐randomised clinical trials, we will consider an additional domain that specifically applies to that design, RoB 2 Domain 1b, 'Bias arising from the timing of identification and recruitment of individual participants within clusters in relation to the timing of randomisation' (https://www.riskofbias.info/). We will follow the suggested algorithm for reaching the risk of bias judgements, for bias arising from the timing of the identification and recruitment of participants in a cluster‐randomised trial.

We will use the RoB 2 Microsoft Excel tool to store the data (it will be available upon request, or an address will be provided in the review).

Measures of treatment effect

If data in a trial are not reported in a format that we can enter directly into a meta‐analysis, we will convert the data to the required format using guidance in Chapter 6 of the Cochrane Handbook for Systematic Reviews of Interventions [75].

Dichotomous outcomes

For dichotomous outcomes, we will calculate the risk ratio (RR) with a 95% confidence interval (CI). For count outcomes (e.g. number of adverse events per individual), we will calculate the rate ratio (i.e. the ratio of the rate in the experimental group to the rate in the control group) with 95% CI.

We will dichotomise time‐to‐event data, if found.

Continuous outcomes

For continuous outcomes, such as health‐related quality of life, we will calculate the mean difference (MD) between the experimental and control groups with a 95% CI if the trials used the same validated tool. If more than one trial measures health‐related quality of life using different validated tools, we will calculate the standardised mean difference (SMD) and 95% CI. The SMD expresses the size of the intervention effect when the MD between groups is divided by the SD amongst participants [75]. As the SMD method does not correct for differences in the direction of the scale, if necessary, we will multiply the mean values from one set of studies by −1 to ensure that all the scale points are in the same direction [75]. We will interpret SMD as follows: SMD less than 0.40 for small intervention effects; SMD between 0.40 and 0.70 for moderate intervention effects; and SMD greater than 0.70 for large intervention effects [76]. We plan to present median and interquartile ranges for continuous data that are not normally distributed (skewed data), in a narrative format. We will present a forest plot to display effect estimates and CIs for individual trials [77]. We will conduct meta‐analyses only when the study groups are sufficiently homogeneous [77].

We will analyse participants in the intervention groups to which they were randomised, regardless of the intervention they received, and we will include all randomised participants in the outcome analyses (i.e. ITT).

Unit of analysis issues

The unit of analysis will be participants with MASLD as originally randomised to the trial groups. We do not expect to find parallel‐group design trials with more than two intervention groups. However, if we identify parallel‐group trials with more than two groups having a common control group, we will divide the control group if it is to be used within the same comparison. We do not expect to find cluster‐randomised or cross‐over trials. However, if we find cluster‐randomised trials, then we will analyse cluster‐randomised trials separately from the randomised parallel‐group clinical trials included in the review as such trials may be at an increased risk of bias [58, 78]. If we find cross‐over trials, then, as already described, we will use only the first trial period for analysis, to avoid the cross‐over effect of the intervention [58].

To avoid repeated observations of study participants, our main analyses will include trial data for the trial participants at the longest follow‐up [75].

Dealing with missing data

If data are missing in a published report, one review author (RE) will contact trial investigators to request the missing data. If trialists have used ITT analysis to deal with missing data, we will use the ITT data. If the required data for ITT analysis are missing in the trial publications, we will use the data as available (i.e. this could be ITT, modified ITT, per‐protocol data, or all of these) in our primary analysis.

As data may be biased (e.g. treatment was withdrawn due to adverse events or participants were excluded from analysis), we will conduct sensitivity analyses as described below. We will include missing data by considering participants as treatment failures or treatment successes, by imputing them according to the following two scenarios.

• Extreme‐case analysis favouring the experimental intervention ('best‐worse' case scenario); none of the dropouts/participants lost from the experimental group, but all the dropouts/participants lost from the control group, experienced the outcome, including all randomised participants in the denominator.

• Extreme‐case analysis favouring the control intervention ('worst‐best' case scenario); all dropouts/participants lost from the experimental group, but none from the control group, experienced the outcome, including all randomised participants in the denominator.

We will perform the two sensitivity analyses only for the critical outcomes.

Reporting bias assessment

If we include 10 or more trials in a meta‐analysis, we will draw funnel plots to assess reporting biases from the individual trials by plotting the RR on a logarithmic scale against its standard error [79, 80]. For dichotomous outcomes, we will test asymmetry using the Harbord test in cases where Tau² is less than 0.1 [81]; we will use the Rücker test if Tau² is more than 0.1 [82]. For continuous outcomes, we will use the regression asymmetry test [79] and the adjusted rank correlation [83].

Synthesis methods

We will perform the meta‐analyses using Review Manager [64], and we will follow the recommendations provided in Chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions [77]. We will perform our meta‐analysis, including outcome data from the trials at any risk of bias.

We will present the results of dichotomous outcomes as RR with 95% CI, and the results of continuous outcomes, such as quality of life, as MD or SMD with 95% CI. In the presence of rare events, we will use the Peto method [77]. We will use random‐effects model meta‐analysis as our primary analyses and the fixed‐effect model meta‐analysis as sensitivity analyses [76, 77]. When it is not appropriate to perform a meta‐analysis, we will present data using forest plots without summary estimates, and we will present a summary of the results. We will follow Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions to identify the most appropriate approach for our review to present findings using other methods [84].

We will address the presence of clinical, methodological, and statistical heterogeneity. We will describe clinical and methodological heterogeneity by exploring the design features of the trial, participants' characteristics, interventions, comparators, outcomes, dropouts and withdrawals, treatment duration, follow‐up, and funding. We will summarise this information, using subheadings, and we will provide a summary of our risk of bias assessments to identify similarities and discrepancies.

We will assess statistical heterogeneity of meta‐analysed trials by visual inspection of forest plots, the Chi² test for heterogeneity, and the I² statistic [85]. For the Chi² test, we will consider a P ≤ 0.10 to indicate statistically significant heterogeneity (i.e. variation in effect estimates beyond that expected by chance). We will use the I² statistic to classify heterogeneity. As thresholds for the interpretation of the I² statistic can be misleading, we will use the following approximate guide for the interpretation of heterogeneity provided in Chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions [77].

• 0% to 40%: might not be important

• 30% to 60%: may represent moderate heterogeneity^a

• 50% to 90%: may represent substantial heterogeneity^a

• 75% to 100%: considerable heterogeneity

^aThe importance of the observed value of the I² statistic depends on the magnitude and direction of effects, and the strength of evidence for heterogeneity (e.g. P value from the Chi² test, or a CI for the I² statistic).

If the heterogeneity is considerable, then we may decide not to meta‐analyse the data.

Investigation of heterogeneity and subgroup analysis

We plan to perform the following subgroup analyses as we expect that they may be a cause for heterogeneity.

• Trials with no for‐profit support compared to trials with for‐profit support, and trials without reported funding. The reason is that trials with vested interests may overestimate beneficial intervention effects or underestimate harmful intervention effects [86].

• Follow‐up at the end of treatment compared to follow‐up at the longest time of follow‐up to determine if the effect of the drugs has been retained or waned.

• Based on the steatosis‐only stage of MASLD compared to metabolic dysfunction‐associated steatohepatitis, and compared to liver cirrhosis, to compare the effect of the drugs in terms of severity of the disease.

We may consider additional subgroup analyses at the review stage.

We will use a formal statistical test in Review Manager to assess subgroup differences that could account for heterogeneity (e.g. Chi² test) [64]. It is recommended to have at least five trials providing data for an outcome in a subgroup to ascertain a valid subgroup difference in effect [77]. We plan to conduct subgroup analyses with two of our critical outcomes (i.e. all‐cause mortality and liver‐related mortality), at the longest follow‐up.

We will use the I² statistic to quantify inconsistencies amongst the trials in each analysis when P value is 0.10 or less. We will also interpret the P value of 0.10 or less from the Chi² test as evidence of statistical heterogeneity [77]. We will use the random‐effects model meta‐analysis to account for the presence of between‐study heterogeneity.

Equity‐related assessment

We do not plan to conduct a formal equity‐related assessment in this review. Our rationale is that the available trial data in this field are unlikely to provide sufficient information disaggregated across PROGRESS‐Plus factors (such as place of residence, race/ethnicity, socioeconomic status, sex, education, occupation, or gender identity). Most trials in this area do not report relevant subgroup analyses or stratified outcome data.

However, we will remain attentive to any equity‐relevant subgroup data that may be reported in the included trials and will extract and report such data where available.

Sensitivity analysis

We plan to perform the below‐listed sensitivity analyses on all our critical and important outcomes (i.e. all‐cause mortality; liver‐related mortality; proportion of people with one or more serious adverse events; liver‐related morbidity; health‐related quality of life; proportion of people with one or more adverse events considered non‐serious; proportion of people with no change in fibrosis or worsening of fibrosis; and proportion of people with no resolution of metabolic dysfunction‐associated steatohepatitis), whenever there are data.

• Restricting the analysis to trials at low risk of bias (see Synthesis methods)

• Restricting the analysis to trials published in an abstract form or unpublished trials, or both

• Conducting the analyses with a fixed‐effect model (see Synthesis methods)

• 'Best‐worst' case scenario analysis (see Dealing with missing data)

• 'Worst‐best' case scenario analysis (see Dealing with missing data)

• Trial Sequential Analysis and assessment of significance. We will compare our assessment of imprecision with GRADE [68] to that performed with the Trial Sequential Analysis [87, 88].

Trial Sequential Analysis

We will conduct Trial Sequential Analysis as cumulative meta‐analyses are at risk of producing random errors due to sparse data and repetitive testing of the accumulating data [65, 66, 67, 89]. To control random errors, we will calculate the diversity‐adjusted required information size (DARIS) (i.e. the number of participants needed in a meta‐analysis to detect or reject a certain intervention effect) [67, 89, 90, 91, 92]. In our dichotomous outcome meta‐analysis, we will base the DARIS on the event proportion in the control group of our meta‐analyses; assumption of a plausible relative risk reduction of 20% or the risk observed in the included trials at low risk of bias; a risk of type I error of 2.5% due to three critical and important secondary outcomes, a risk of type II error of 10% [87], and the diversity of the included trials in the meta‐analysis. For our continuous outcome meta‐analysis (health‐related quality of life), we will estimate DARIS using the SD observed in the control group and the minimal relevant difference of 50% of this SD; alpha of 2.5% due to three important outcomes [93]; beta of 10% [87]; and the diversity as estimated from the trials in the meta‐analysis [94]. We will also calculate and report the Trial Sequential Analysis‐adjusted 95% CI if the cumulative Z‐score does not cross any of the trial sequential monitoring boundaries for benefit, harm, or futility [65, 67]. The underlying assumption of Trial Sequential Analysis is that testing for statistical significance may be performed each time a new trial is added to the meta‐analysis. We will add the trials according to the year of publication, and, if more than one trial has been published in a year, we will add trials alphabetically according to the last name of the first author. Based on the DARIS, we will construct the trial sequential monitoring boundaries for benefit, harm, and futility [65, 67, 89]. These boundaries will determine the statistical inference one may draw regarding the cumulative meta‐analysis that has not reached the DARIS; if the trial sequential monitoring boundary for benefit or harm is crossed before the DARIS is reached, firm evidence for an intervention effect may be established, and further trials may be superfluous. However, if the boundaries are not crossed, it is most probably necessary to continue doing trials to detect or reject a certain intervention effect. If the cumulative z‐curve crosses the trial sequential monitoring boundaries for futility, no more trials may be needed. A more detailed description of Trial Sequential Analysis can be found at https://www.ctu.dk/tsa/ [65, 66, 67]. We will perform Trial Sequential Analysis with Trial Sequential Analysis software, version 0.9.5.10 beta [66]. We will use random‐effects meta‐analysis.

Downgrading for imprecision with Trial Sequential Analysis

In Trial Sequential Analysis where the cumulative z‐value does not cross the monitoring boundaries for benefit, harm, or futility, we will downgrade our assessment of imprecision by three levels if the accrued number of participants is below 33% of the DARIS, by two levels if between 33% and 65%, and by one level if between 66% and 99% of DARIS. We will not downgrade for imprecision if the cumulative z‐value reaches or crosses benefit, harm, futility, or DARIS.

Certainty of the evidence assessment

We will create two summary of findings tables with the following comparisons.

• Any bile acid administered at any dose or regimen versus no intervention or placebo

• Any bile acid administered at any dose or regimen versus another bile acid administered at any dose or regimen

In both tables, we will present the outcomes: all‐cause mortality; liver‐related mortality; proportion of people with one or more serious adverse events; liver‐related morbidity; health‐related quality of life; and proportion of people with one or more adverse events considered non‐serious.

The GRADE approach appraises the certainty of a body of evidence based on the extent to which one can be confident that an estimate of effect or association reflects the item being assessed [95]. The certainty of a body of evidence considers within‐study risk of bias, indirectness of the evidence, heterogeneity of the data, imprecision of effect estimates, and risk of publication bias [96, 97, 98, 99, 100, 101, 102, 103, 104, 105, 106, 107, 108, 109, 110, 111].

Regarding risk of bias, we will use the overall judgement for the result of an outcome. Low risk of bias indicates no limitation (the certainty is not downgraded); some concerns indicates either no limitation or serious limitation (the certainty is downgraded one level); and high risk of bias indicates either serious limitation or very serious limitation (the certainty is downgraded two levels) [95]. For the assessment of imprecision, we will use the latest guidance based on the use of a minimally contextualised approach which is based on thresholds and CI of absolute effects as the primary criterion for imprecision rating (i.e. the CI approach) [112]. The primary considerations for this include the following.

• If the CIs are wide and considerably crossed prespecified thresholds of interest (we will consider 0.25 as trivial), we will downgrade two levels for imprecision, and if the CIs are very wide and both boundaries of the CIs suggest very different inferences, we will consider downgrading three levels.

• If the CIs do not cross the threshold and the relative effect is large, we will consider implementing the optimal information size (OIS) approach, downgrading more than one level for imprecision if the sample size of the meta‐analysis is far less than the OIS.

We will interpret the GRADE Working Group grades of evidence as follows.

• High certainty: we are very confident that the true effect lies close to that of the estimate of the effect.

• Moderate certainty: we are moderately confident in the effect estimate: the true effect is likely to be close to the estimate of the effect, but there is a possibility that it is substantially different.

• Low certainty: our confidence in the effect estimate is limited: the true effect may be substantially different from the estimate of the effect.

• Very low certainty: we have very little confidence in the effect estimate: the true effect is likely to be substantially different from the estimate of effect.

Two review authors (RE and PA) will independently conduct GRADE assessments using GRADEpro GDT [68]. The two review authors will resolve any discrepancies through discussion with a third review author (CP, OB, or CG). We will justify all decisions to downgrade the certainty of the evidence for each outcome in footnotes, and we will make comments to aid readers' understanding of our judgements if necessary.

We will conduct the review according to this protocol. We will report any deviations from it in the 'Methods' section.

Consumer involvement

One of the co‐authors of this protocol (PA) has previously been listed as a consumer representative in the Editorial Manager system and contributed to this protocol from the perspective of someone with lived experience relevant to MASLD.

Supporting Information

Supplementary materials are available with the online version of this article: 10.1002/14651858.CD014850.

Supplementary materials are published alongside the article and contain additional data and information that support or enhance the article. Supplementary materials may not be subject to the same editorial scrutiny as the content of the article and Cochrane has not copyedited, typeset or proofread these materials. The material in these sections has been supplied by the author(s) for publication under a Licence for Publication and the author(s) are solely responsible for the material. Cochrane accordingly gives no representations or warranties of any kind in relation to, and accepts no liability for any reliance on or use of, such material.

Supplementary material 1 Search strategies

New

Additional information

Contributions of authors

REA: conceptualisation, project administration, methodology, writing of original draft, investigation, and writing – review and editing.

OB: writing – review and editing.

DN: conceptualisation, methodology, investigation, supervision, and writing – review and editing.

CP: conceptualisation, methodology, supervision, writing and reviewing the protocol.

PA: writing – review and editing.

CG: conceptualisation, methodology, investigation, supervision, writing – review and editing.

All authors approved the current version for publication.

Declarations of interest

REA: none.

OB: none.

DN is the Managing Editor of the Cochrane Hepato‐Biliary Group (CHBG).

CP is a CHBG Editor.

CG is the Co‐ordinating Editor of the CHBG.

PA is a CHBG Editor and external CHBG consumer peer reviewer.

The authors, DN, CP, PA, and CG, are Cochrane Editors but were not involved in the editorial process of this article.

Sources of support

Internal sources

• The Cochrane Hepato‐Biliary Group Editorial Team office, Denmark

  DN: is paid by the Danish State in the form of a monthly salary through the Rigshospitalet, which hosts the Cochrane Hepato‐Biliary Group (CHBG) Editorial Team office.

  CG: is paid by the Danish State in the form of a monthly salary through the Rigshospitalet, which hosts the CHBG Editorial Team office.

• The Cochrane Hepato‐Biliary Group, Denmark

  Design of search strategies

External sources

• The Cochrane Hepato‐Biliary Group, Denmark

  Design of search strategies

Registration and protocol

Not relevant

Data, code and other materials

Data sharing is not applicable to this article as it is a protocol, so no datasets were generated or analysed.