Essential phospholipids for people with non‐alcoholic fatty liver disease

Abstract

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

To assess the benefits and harms of essential phospholipids in adults with non‐alcoholic fatty liver disease (NAFLD).

Background

Description of the condition

Non‐alcoholic fatty liver disease (NAFLD) covers conditions related to accumulation of fat in the liver if specific causes, such as significant alcohol consumption, long‐term use of a steatogenic medication, or monogenic hereditary disorders can be excluded (WGO 2014). Non‐alcoholic fatty liver disease features a wide spectrum of histologically conditions, from simple accumulation of fat (‘fatty liver’ or hepatic steatosis) to non‐alcoholic steatohepatitis (NASH), liver fibrosis, and liver cirrhosis with clinical consequences (Brunt 2011; McPherson 2015; Bertot 2016). Simple hepatic steatosis is defined as when the fat, built up in the epithelial cells of the liver, is at least 5% of the liver weight, and the parenchymal cells and liver structure are intact. Non‐alcoholic fatty liver (NAFL) is defined as the presence of hepatic steatosis with no evidence of hepatocellular injury in the form of ballooning of the hepatocytes. Non‐alcoholic steatohepatitis is defined as the presence of hepatic steatosis and inflammation with hepatocyte injury (ballooning) with or without fibrosis (Brunt 2011). Non‐alcoholic fatty liver disease is considered to be a clinical manifestation of the metabolic syndrome, that is the co‐occurrence of metabolic risk factors for both type 2 diabetes and cardiovascular disease (abdominal obesity, hyperglycaemia, dyslipidaemia, and hypertension) (Dyson 2014; Mikolasevic 2016; AASLD NAFLD 2018). The prevalence of NAFLD is increasing, but only a small number of affected people develop inflammation, which may be followed by fibrosis and cirrhosis, possibly requiring liver transplantation (Bertot 2016; Younossi 2016). The life expectancy in people with hepatic steatosis is reported to be similar to the life expectancy of the general population (Lazo 2011).

The pathogenesis of NAFLD remains unclear, and none of the theories proposed so far can explain its pathogenesis. Two popular theories are the 'two‐hit' hypothesis, which has failed in its attempt to explain the several molecular and metabolic changes occurring in NAFLD (Dowman 2010), and the 'multiple‐hit' hypothesis, which proposes that multiple injuries act together and induce NAFLD in people who are genetically predisposed to acquire it (Buzzetti 2016; Borrelli 2018). The gut microbiota participate in the mechanism of insulin resistance which increases influx of free fatty acids to the liver, activates endoplasmic reticulum stress, oxidative stress, and mitochondrial dysfunction, which results in an overproduction of reactive oxygen species, abnormal functioning of cell membranes, consequent activation of inflammatory response, cell injury, apoptosis, and cell death (Buzzetti 2016). Studies have shown that changes in gut microbiota may have an impact on pathogenesis and lipotoxicity of NASH as well as other diseases (Marra 2018), but the making of simple associations may be misinterpreted (Cani 2018). However, results from genetic studies have shown that epigenetic factors interacting with genetic risk variants may predict development of aggressive phenotypes in NAFLD such as cirrhosis and hepatocellular carcinoma (HCC) (Eslam 2018).

Non‐alcoholic fatty liver disease diagnosis is established by excluding excessive alcohol use and other forms of liver disease by history and laboratory tests (EASL NAFLD 2016; AASLD NAFLD 2018). Hepatic steatosis is primarily diagnosed by ultrasound screening, transient elastography (Kwok 2016), or by the use of more sensitive non‐invasive imaging methods like proton magnetic resonance spectroscopy or quantitative fat/water selective magnetic resonance imaging (Middleton 2017), or by liver biopsy (Ratziu 2005).

Non‐alcoholic fatty liver disease prevalence ranges from 7% to 43% in adult individuals worldwide based on epidemiological data, given that in people with type 2 diabetes (over 76%) or obesity (over 90% in severely obese individuals) the prevalences of NAFLD are much higher (Younossi 2016). Prevalence depends on ethnicity, age, sex, obesity, and physical activities (Browning 2004; Koehler 2012; AASLD NAFLD 2018). Non‐alcoholic fatty liver disease is more often observed in Hispanic and Mexican populations compared to non‐Hispanic whites and African‐Americans (Fleischman 2014; Kalia 2016). Most often, people at high risk are men and postmenopausal women, Ballestri 2017, or those with high body mass index, Bedogni 2005, or those with low physical activity Frith 2010.

Description of the intervention

Essential phospholipids have been administered to people with fatty liver since 1988 due to their antioxidant, anti‐inflammatory, and apoptosis‐modulating effects (Gundermann 2011). Essential phospholipids contain extract of polyenylphosphatidylcholine molecules from soybean with 73% to 96% of 3‐sn‐phosphatidylcholine, with a high content of bound polyunsaturated fatty acids. Essential phospholipids are primarily incorporated into high‐density lipoproteins and into all membrane‐containing cell structures of hepatocytes (LeKim 1976; Zierenberg 1981). The Russian RSLS NASH 2015 guidelines, based on beneficial results of 5 randomised clinical trials, recommend the administration of 1800 mg per day (2 capsules thrice a day) of essential phospholipids for 12 to 24 weeks.

How the intervention might work

Phospholipids are essential components of the cell membranes and form the double layer of cellular and subcellular membranes (Cushley 2002). The composition of phospholipids influence the membrane fluidity, permeability, and the membrane‐dependent metabolic processes between the intracellular and intercellular space; modulate membrane‐associated enzymatic activities; and provide a matrix for the assembly and function of a variety of catalytic processes (Gundermann 2011; Paradies 2014). The exact mechanisms through which essential phospholipids work are unknown.

Why it is important to do this review

Treatment of people with NAFLD is far from optimal. Contemporary guidelines recommend healthy diet, physical activity, and weight loss, but data for effective pharmacological treatment are insufficient (Lombardi 2017). Guidelines in Eastern European countries recommend essential phospholipids for people with NASH (RSLS NASH 2015), and in 2017, essential phospholipids alone and combined with other molecules accounted for 46.9% of the 'hepatoprotective' drugs market in Russia (Polyanichko 2018).

We found one meta‐analysis from 1998 that included data from nine randomised clinical trials and one systematic review with meta‐analysis published in 2005 (Gundermann 1998; Hu 2005), both of which assessed phospholipids in people with chronic liver disease. The latter study contained data from six randomised clinical trials and concluded that essential phospholipids had positive effects on histological as well as laboratory outcomes. However, the included trial participants in this review had chronic liver disease of different aetiologies such as alcoholic fatty liver, non‐alcoholic fatty liver disease, viral hepatitis B, or viral hepatitis C (Hu 2005). Gundermann and colleagues published a review of the literature, describing the results of the individual randomised and various non‐randomised studies (Gundermann 2011). An update of this review followed in 2016 (Gundermann 2016). The studied population were people with alcoholic and non‐alcoholic fatty liver disease. No meta‐analysis was performed. A Cochrane Review including GRADE assessment of the evidence is thus required to assess the benefits and harms of essential phospholipids in adults with NAFLD.

Objectives

To assess the benefits and harms of essential phospholipids in adults with non‐alcoholic fatty liver disease (NAFLD).

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised clinical trials for assessment of benefits and harms, no matter the language, publication status, or year of publication. If, during the selection of trials, we identify observational studies (i.e. quasi‐randomised studies, cohort studies, or patient reports) that report adverse events associated with essential phospholipids, we will review these studies for report on adverse events. We will not specifically search for observational studies for inclusion in this review, which is a known limitation of this review. We are aware that the decision not to search for all observational studies might bias our review towards assessment of benefits and might overlook certain harms such as late or rare harms. If we demonstrate benefits from the use of essential phospholipids in adults with NAFLD, then a systematic review of harms of essential phospholipids in adults with NAFLD in observational studies ought to be launched (Storebø 2018). We will not analyse the extracted data on harms from non‐randomised clinical studies together with the data on harms from the randomised clinical trials included in the review; neither we will assess the bias risk in these studies. However, we will refer to the extracted narrative data on harm with a link to the table in an Appendix, or alternatively, we may present a narrative analysis at the end of the Results section.

Types of participants

Inclusion criteria

We will include adult participants (18 years of age and above) diagnosed with NAFLD at any stage, that is NAFL with or without NASH, and with or without liver fibrosis or cirrhosis likely due to NAFL or NASH.

Exclusion criteria

We will exclude randomised clinical trials in which participants are coinfected with hepatitis B, hepatitis C, or HIV infection.

Types of interventions

Experimental

Peroral or parenteral essential phospholipids at any dose and duration. We will also include phospholipid preparations combined with other molecules (e.g. silybin phytosome complex (silybin plus phosphatidylcholine) coformulated with vitamin E; glycyrrhizic acid with phospholipids).

Control

Placebo or no intervention.

We will allow cointerventions in the intervention group if the cointervention is administered equally to the comparison group.

Types of outcome measures

Primary outcomes

• Proportion of people with one or more serious adverse events during treatment. We will use the International Conference on Harmonisation (ICH) Guidelines for Good Clinical Practice's definition of a serious adverse event (ICH‐GCP 1997), that is 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. We will assess the proportion of participants with one or more serious adverse events. We will use the definitions employed by the study authors for serious adverse events.

• Health‐related quality of life (we will consider the data if trialists used validated scales).

• Histological response (proportion of trial participants without histological improvement in the degree of fatty liver infiltration, inflammation, and fibrosis) based on any validated score systems.

Secondary outcomes

• All‐cause mortality.

• Proportion of people with one or more adverse events considered not to be serious (see above).

Exploratory outcomes

• Participants without a decrease of liver enzymes.

• Separately reported serious adverse events.

• Separately reported non‐serious adverse events.

We will analyse the proportion of trial participants for each outcome, and separately for the following time points: end of treatment (for all our primary, secondary, and exploratory outcomes) and at the longest follow‐up (for all our primary and secondary outcomes). However, we will base our primary conclusions on the outcomes measured at end of treatment.

Search methods for identification of studies

Electronic searches

We will search The Cochrane Hepato‐Biliary Group Controlled Trials Register (Cochrane Hepato‐Biliary Group Module), Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library, MEDLINE Ovid, Embase Ovid, LILACS (BIREME) (Latin American and Caribbean Health Science Information database), Science Citation Index Expanded (Web of Science), and Conference Proceedings Citation Index – Science (Web of Science) (Royle 2003). We will apply no language or document type restrictions. The preliminary search strategies with the expected time spans of the searches are shown in Appendix 1.

Searching other resources

We will handsearch the reference lists of articles from the computerised databases and relevant review articles to identify additional references. We will search online trial registries such as the US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (clinicaltrials.gov), European Medicines Agency (www.ema.europa.eu/ema/), World Health Organization International Clinical Trials Registry Platform (www.who.int/ictrp), the US Food and Drug Administration (www.fda.gov), eLibrary, VINITI, Russian Medicine, and pharmaceutical company sources for ongoing or unpublished trials.

We will attempt to search Chinese databases through the Chinese Cochrane Center.

Data collection and analysis

We will follow the guidelines provided in the Cochrane Handbook for Systematic Reviews of Interventions,Higgins 2011, and The Cochrane Hepato‐Biliary Group Module (Cochrane Hepato‐Biliary Group Module). We will perform the analyses using Review Manager 5, Review Manager 2014, and Trial Sequential Analysis (Thorlund 2011; TSA 2011; Wetterslev 2017). We will assess the evidence according to Jakobsen and colleagues (Jakobsen 2014).

Selection of studies

We will retrieve publications that we consider to be potentially eligible for inclusion after reading their abstracts, and review articles that may provide useful references for studies. Two review authors (DLV and CP) will independently review the publications for eligibility. DLV and CP will independently assess the full text of each publication to determine if the trial participants and the interventions administered meet the inclusion criteria of this protocol. We will only include abstracts if sufficient data are provided for analysis. Any disagreements will be resolved by discussion or by involving any of the remaining authors for arbitration.

Data extraction and management

Two review authors (DLV and CP) will independently extract data from the trials fulfilling the protocol inclusion criteria, using a pre‐piloted data extraction form. Extracted trial information will include:

• publication data (i.e. title, year (range of years) of conductance of the trial and language of publication, place and country of the recruited participants, authors);

• study design;

• funding;

• setting, inclusion and exclusion criteria, methods of randomisation, allocation concealment, and blinding;

• sample size calculation performed and reached, or not;

• population data (i.e. age, sex, ethnicity, history of the disease);

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

• outcomes;

• dropouts and reasons for it;

• length of follow‐up;

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

• number of participants randomised;

• number of participants included for 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;

• harms reported in non‐randomised studies.

The review authors will ensure that they have retrieved and collected all required available data from the trial publications and through contact with authors. Any disagreements between review authors will be resolved by discussion.

Assessment of risk of bias in included studies

Two review authors (DLV and CP) will independently assess the risk of bias of each included trial according to the recommendations in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), the Cochrane Hepato‐Biliary Group Module, and methodological studies (Schulz 1995; Moher 1998; Kjaergard 2001; Rücker 2008; Wood 2008; Savović 2012a; Savović 2012b; Lundh 2017; Savović 2018). We will use the following definitions in the assessment of risk of bias.

Allocation sequence generation

• Low risk of bias: the study authors performed sequence generation using computer random number generation or a random number table. Drawing lots, tossing a coin, shuffling cards, and throwing dice are adequate if performed by an independent person not otherwise involved in the study. In general, we will classify the risk of bias as low if the method used for allocation concealment suggested that it was extremely likely that the sequence was generated randomly (e.g. use of interactive voice response system).

• Unclear risk of bias: the study authors did not specify the method of sequence generation.

• High risk of bias: the sequence generation method was not random. We will exclude such quasi‐randomised studies.

Allocation concealment

• Low risk of bias: the participant allocations could not have been foreseen in advance of, or during, enrolment. A central and independent randomisation unit controlled allocation. The investigators are unaware of the allocation sequence (e.g. if the allocation sequence was hidden in sequentially numbered, opaque, and sealed envelopes).

• Unclear risk of bias: the study authors did not describe the method used to conceal the allocation so that the intervention allocations may have been foreseen before, or during, enrolment.

• High risk of bias: it is likely that the investigators who assigned the participants knew the allocation sequence. We will exclude such quasi‐randomised studies.

Blinding of participants and personnel

• Low risk of bias: blinding of participants and key study personnel is ensured, and it was unlikely that the blinding could have been broken; or rarely no blinding or incomplete blinding, but the review authors judged that the outcome was not likely to have been influenced by lack of blinding.

• Unclear risk of bias: either of the following: insufficient information to permit a judgement of 'low risk' or 'high risk'; or the trial did not address this outcome.

• High risk of bias: either of the following: no blinding or incomplete blinding, and the outcome was likely to have been influenced by lack of blinding; or blinding of key study participants and personnel attempted, but it is likely that the blinding could have been broken, and the outcome was likely to have been influenced by lack of blinding.

Blinded outcome assessment

• Low risk of bias: blinding of outcome assessment is ensured, and it was unlikely that the blinding could have been broken; or rarely no blinding of outcome assessment, but the review authors judged that the outcome measurement was not likely to have been influenced by lack of blinding.

• Unclear risk of bias: either of the following: insufficient information to permit judgement of 'low risk' or 'high risk'; or the trial did not address this outcome.

• High risk of bias: either of the following: no blinding of outcome assessment, and the outcome measurement was likely to have been influenced by lack of blinding; or blinding of outcome assessment, but it is likely that the blinding could have been broken, and the outcome measurement was likely to have been influenced by lack of blinding.

Incomplete outcome data

• Low risk of bias: missing data were unlikely to make treatment effects depart from plausible values. The study used sufficient methods, such as multiple imputation, to handle missing data.

• Unclear risk of bias: there was insufficient information to assess whether missing data in combination with the method used to handle missing data were likely to induce bias on the results.

• High risk of bias: the results were likely to be biased due to missing data.

Selective outcome reporting

• Low risk: the trial should report the following of our predefined primary outcomes: serious adverse events, health‐related quality of life, and histological response. If the original trial protocol was available, the outcomes should be those called for in that protocol. If the trial protocol was obtained from a trial registry (e.g. ClinicalTrials.gov), the outcomes sought should be those enumerated in the original protocol if the trial protocol was registered before or at the time that the trial was begun. If the trial protocol was registered after the trial was begun, those outcomes are not considered to be reliable.

• Unclear: not all predefined outcomes were reported fully, or it was unclear whether data on these outcomes were recorded or not.

• High risk: one or more predefined outcomes were not reported.

Other bias

• Low risk of bias: the trial appeared to be free of other components that could put it at risk of bias (e.g. baseline differences, early stopping).

• Unclear risk of bias: the trial may or may not have been free of other components that could put it at risk of bias.

• High risk of bias: there were other factors in the trial that could put it at risk of bias (e.g. baseline differences, early stopping).

Bias at outcome level

We will classify an outcome to be at a low risk of bias if blinding of participants, healthcare professionals, and outcome assessors; incomplete outcome data; and selective outcome reporting domains are at low risk of bias (Savović 2018).

Overall bias assessment

• Low risk of bias: all domains were classified as low risk of bias using the definitions described above.

• High risk of bias: one or more of the bias domains were classified as unclear or high risk of bias.

Measures of treatment effect

Dichotomous outcomes

For dichotomous outcomes, we will calculate the risk ratio (RR) with 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 intervention group to the rate in the control group) with 95% CI.

Continuous outcomes

For continuous outcomes, we will calculate the mean difference (MD) between the experimental and control groups with a 95% CI. If more than one study measures health‐related quality of life using different tools, we will calculate the standardised mean difference (SMD) with 95% CI.

Unit of analysis issues

The unit of analysis will be participants with NAFLD as originally randomised to the trial groups. We do not expect to find parallel‐group design trials with more than two intervention groups. We do not expect to find cluster‐randomised or cross‐over trials. However, if we find cluster‐randomised trials, then we will analyse and assess the risk of bias of cluster‐randomised trials separately from the randomised parallel‐group clinical trials included in the review (Higgins 2011). If we find cross‐over trials, then we will use for analysis only the first trial period in order to avoid the cross‐over effect of the intervention (Higgins 2011).

Dealing with missing data

If dichotomous or continuous data are missing in a published report, we will, whenever possible, contact the original investigators to request the missing data. If trialists used intention‐to‐treat analysis to deal with missing data, we will use these data in our primary analysis. If the required data for intention‐to‐treat analysis are missing, we may not be able to perform such an analysis, and we will use the data as found in the trial publications, that is we will use per‐protocol analyses. Since these may be biased (e.g. treatment was withdrawn due to adverse events or participants were excluded from analysis), we will conduct the best‐worst case scenario analysis described below as sensitivity analyses whenever possible for dichotomous outcomes.

Dealing with missing data using sensitivity analysis

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 participants who dropped out from the experimental group experienced the outcome, but all of the participants who dropped out from the control group experienced the outcome; including all randomised participants in the denominator.

• 'Extreme‐case' analysis favouring the control (’worst‐best’ case scenario): all participants who dropped out 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 all‐cause mortality and serious adverse events.

Assessment of heterogeneity

We will address the presence of heterogeneity in clinical, methodological, and statistical ways. To assess heterogeneity between the trials, we will specifically examine the degree of heterogeneity observed in the results using the I² statistic (Higgins 2002). As thresholds for the interpretation of I² can be misleading, we will use the following rough guide for interpretation of heterogeneity provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011):

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity*;

• 50% to 90%: may represent substantial heterogeneity*;

• 75% to 100%: considerable heterogeneity*.

*The importance of the observed value of I² depends on (i) the magnitude and direction of effects, and (ii) the strength of evidence for heterogeneity (e.g. P value from the Chi² test, or a CI for I²). For the heterogeneity adjustment of the required information size in the Trial Sequential Analysis, we will use diversity (D²) because the I² statistics used for this purpose consistently underestimate the required information size (Wetterslev 2009).

Assessment of reporting biases

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 (Egger 1997; Higgins 2011). For dichotomous outcomes, we will test asymmetry using the Harbord test in cases where Tau² is less than 0.1 (Harbord 2006); we will use Rücker 2008 in cases where Tau² is more than 0.1. For continuous outcomes, we will use the regression asymmetry test, Egger 1997, and the adjusted rank correlation (Begg 1994).

Data synthesis

Meta‐analysis

We will perform the meta‐analyses using Review Manager 5 (Review Manager 2014), and according to the recommendations provided in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will present the results of dichotomous outcomes of individual trials as RR with 95% CI, and the results of continuous outcomes as MD or SMD for health‐related quality of life with 95% CI.

Assessment of significance

We will present the results of dichotomous outcomes of individual trials as RR with 95% CI, and the results of continuous outcomes as MD with 95% CI. We will apply both fixed‐effect model, DeMets 1987, and random‐effects model, DerSimonian 1986, meta‐analyses. If there are statistically significant discrepancies in the results (e.g. one model giving a significant intervention effect and the other no significant intervention effect), we will report the more conservative point estimate of the two models (Jakobsen 2014). The more conservative point estimate is the estimate closest to zero effect. If the two point estimates are equal, we will use the estimate with the widest CI as our main result of the two analyses. We will consider a P value of 0.025 or less, two‐tailed, as statistically significant if the required information size is reached due to the three primary outcomes at end of treatment (Jakobsen 2014). We will use the eight‐step procedure to assess if the thresholds for significance are crossed (Jakobsen 2014). We will present heterogeneity using the I² statistic (Higgins 2002). We will present the results of the individual trials and meta‐analyses in the form of forest plots. Where data are only available from one trial, we will use Fisher’s exact test for dichotomous data, Fisher 1922, and Student’s t test for continuous data, Student 1908, to present the results narratively.

Trial Sequential Analysis

We will apply Trial Sequential Analysis for both dichotomous and continuous primary and secondary outcomes (Thorlund 2011; TSA 2011; Wetterslev 2017), as cumulative meta‐analyses are at risk of producing random errors due to sparse data and repetitive testing of the accumulating data (Wetterslev 2008). 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) (Brok 2008; Wetterslev 2008; Brok 2009; Thorlund 2010; Wetterslev 2017). In our dichotomous outcome meta‐analysis, we will base the DARIS on the event proportion in the control group; 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 primary outcomes and a risk of type I error of 3.3% due to two secondary outcomes (Jakobsen 2014), a risk of type II error of 10% (Castellini 2018), and the diversity of the included trials in the meta‐analysis. For our continuous outcome meta‐analyses, 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 the primary outcomes (Jakobsen 2014); beta of 10% (Castellini 2018); and the diversity as estimated from the trials in the meta‐analysis (Wetterslev 2009). 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 (Thorlund 2011; Wetterslev 2017).

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 (Wetterslev 2008; Thorlund 2011; Wetterslev 2017). 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. However, 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 www.ctu.dk/tsa/ (Thorlund 2011; TSA 2011; Wetterslev 2017).

Subgroup analysis and investigation of heterogeneity

We will perform the following subgroup analyses whenever possible:

• trials at overall low risk of bias compared to trials at overall high risk of bias;

• trials without for‐profit funding compared to trials with for‐profit funding;

• follow‐up at the end of treatment compared to follow‐up at the longest time point;

• based on stage of NAFLD: non‐alcoholic fatty liver, non‐alcoholic steatohepatitis, liver fibrosis, or liver cirrhosis.

• trials with peroral essential phospholipids compared to trials with parenteral essential phospholipids administration;

• trials with essential phospholipids only compared to trials with phospholipid preparations combined with other molecules.

We may consider additional subgroup analyses at the review stage. Due to the large number of subgroup analyses, we will interpret them conservatively.

Sensitivity analysis

The specified sensitivity analyses are provided in the Dealing with missing data section.

In addition to the sensitivity analysis described in the Dealing with missing data section, we plan to compare our assessment of imprecision using GRADE to that performed using the Trial Sequential Analysis (Castellini 2018; Gartlehner 2018).

’Summary of findings’ tables

We will create ’Summary of findings’ tables on our primary and secondary outcomes using GRADEpro GDT 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 (Schünemann 2013). 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 (Guyatt 2008; Balshem 2011; Guyatt 2011a; Guyatt 2011b; Guyatt 2011c; Guyatt 2011d; Guyatt 2011e; Guyatt 2011f; Guyatt 2011g; Guyatt 2011h; Mustafa 2013; Guyatt 2013a; Guyatt 2013b; Guyatt 2013c; Guyatt 2013d; Guyatt 2017).

We will define the levels of evidence as ’high’, ’moderate’, ’low’, or ’very low’.

GRADE Working Group grades of evidence

• 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.

Appendices

Appendix 1. Search strategies

Database	Time of search	Search strategies
The Cochrane Hepato‐Biliary Group Controlled Trials Register	Date will be given at review stage.	(phospholipid* or EPL or phosphatidylcholine*) AND ((non*alcoholic and (fatty liver or steatohepatitis)) or NAFL* or NASH*)
Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library	Latest issue	#1 MeSH descriptor: [Phospholipids] explode all trees #2 phospholipid* or EPL or phosphatidylcholine* #3 #1 or #2 #4 MeSH descriptor: [Non‐alcoholic Fatty Liver Disease] explode all trees #5 (non*alcoholic and (fatty liver or steatohepatitis)) or NAFL* or NASH* #6 #4 or #5 #7 #3 and #6
MEDLINE Ovid	1946 to the date of search	1. exp Phospholipids/ 2. (phospholipid* or EPL or phosphatidylcholine*).mp. [mp=title, abstract, original title, name of substance word, subject heading word, keyword heading word, protocol supplementary concept word, rare disease supplementary concept word, unique identifier] 3. 1 or 2 4. exp Non‐alcoholic Fatty Liver Disease/ 5. ((non*alcoholic and (fatty liver or steatohepatitis)) or NAFL* or NASH*).mp. [mp=title, abstract, original title, name of substance word, subject heading word, keyword heading word, protocol supplementary concept word, rare disease supplementary concept word, unique identifier] 6. 4 or 5 7. 3 and 6 8. (random* or blind* or placebo* or meta‐analys*).mp. [mp=title, abstract, original title, name of substance word, subject heading word, keyword heading word, protocol supplementary concept word, rare disease supplementary concept word, unique identifier] 9. 7 and 8
Embase Ovid	1974 to the date of search	1. exp phospholipid/ 2. (phospholipid* or EPL or phosphatidylcholine*).mp. [mp=title, abstract, heading word, drug trade name, original title, device manufacturer, drug manufacturer, device trade name, keyword, floating subheading] 3. 1 or 2 4. exp nonalcoholic fatty liver/ 5. ((non*alcoholic and (fatty liver or steatohepatitis)) or NAFL* or NASH*).mp. [mp=title, abstract, heading word, drug trade name, original title, device manufacturer, drug manufacturer, device trade name, keyword, floating subheading] 6. 4 or 5 7. 3 and 6 8. (random* or blind* or placebo* or meta‐analys*).mp. [mp=title, abstract, heading word, drug trade name, original title, device manufacturer, drug manufacturer, device trade name, keyword, floating subheading] 9. 7 and 8
LILACS (BIREME)	1982 to the date of search	(phospholipid$ or EPL or phosphatidylcholine$) [Words] and ((non$alcoholic and (fatty liver or steatohepatitis)) or NAFL$ or NASH$) [Words]
Science Citation Index Expanded (Web of Science)	1900 to the date of search	#5 #4 AND #3 #4 TS=(random* or blind* or placebo* or meta‐analys*) #3 #2 AND #1 #2 TS=((non*alcoholic and (fatty liver or steatohepatitis)) or NAFL* or NASH*) #1 TS=(phospholipid* or EPL or phosphatidylcholine*)
Conference Proceedings Citation Index – Science (Web of Science)	1990 to the date of search	#5 #4 AND #3 #4 TS=(random* or blind* or placebo* or meta‐analys*) #3 #2 AND #1 #2 TS=((non*alcoholic and (fatty liver or steatohepatitis)) or NAFL* or NASH*) #1 TS=(phospholipid* or EPL or phosphatidylcholine*)

Contributions of authors

DLV: drafted the protocol CP: drafted and revised the protocol GC: drafted and revised the protocol DN: drafted and revised the protocol CG: drafted and revised the protocol

All authors agreed on the current protocol version for publication.

Sources of support

Internal sources

• None, Other.

External sources

• None, Other.

Declarations of interest

DLV: none known. CP is Vice‐president of the Russian Scientific Liver Society; in 2016 CP received direct funding from Sanofi for work related to the DIREG 02 study, an observational study examining the prevalence of non‐alcoholic fatty liver disease in Russia. Sanofi manufactures ESSENTIALE (essential phospholipids). Also in 2016, CP was invited by Sanofi, Russia, through the Russian Liver Scientific Society, to deliver clinical lectures on epidemiology, pathogenesis, diagnostic options, and treatment of non‐alcoholic fatty liver disease. The work on this protocol is outside the declared conflicts of interest. GC: none known. DN is Managing Editor of The Cochrane Hepato‐Biliary Group. CG is Co‐ordinating Editor of The Cochrane Hepato‐Biliary Group.

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