Types of studies

All randomised trials regardless of publication status, language, or blinding. We will include unpublished trials if the methodology and the data could be accessed in written form.

Types of participants

Patients with hepatic encephalopathy in connection with acute or chronic liver diseases or fulminant hepatic failure will be included. Patients will be included regardless of their of sex, age, ethnic origin, or the etiology of the liver disease and the factor(s) precipitating the hepatic encephalopathy. Due to the wide spectrum of symptoms and underlying liver failure, hepatic encephalopathy would traditionally been divided into three categories.

Acute hepatic encephalopathy involves an abrupt onset of neuropsychiatric symptoms in patients with chronic liver disease. Acute hepatic encephalopathy may be idiopathic or precipitated by one or more causes including infections, gastrointestinal bleeding, electrolyte or acid‐base disturbances, constipation, medications, hypo‐ or hyperglycaemia, renal dysfunction, large protein meals, alcohol withdrawal, or a superimposed acute liver disease (Als‐Nielsen 2004).

Chronic hepatic encephalopathy involves persistent neuropsychiatric dysfunction in patients with chronic liver disease. The onset is usually insidious and the dysfunction may be clinically overt (ie, chronic hepatic encephalopathy) or only demonstrable by psychometric testing (ie, minimal hepatic encephalopathy also known as subclinical or latent hepatic encephalopathy) (Als‐Nielsen 2004).

Fulminant hepatic failure is a severe stage of hepatic functional deterioration in patients without underlying liver disease. The main clinical features are hepatic encephalopathy and direct symptoms of liver cell damage, mainly jaundice and coagulation disorders (Bernuau 1999).

Types of interventions

Naloxone in any dose or duration compared with placebo or with no intervention. Additional interventions will be allowed, if received equally by all intervention and control groups.

Types of outcome measures

Selection of studies

The selection of trials will be undertaken by three authors (SUN, YIN, and JING). The search strategy described will be used to obtain titles and abstracts of trials that may be relevant to the review. The titles and abstracts will be screened independently by SUN and YIN. The authors will discard the inapplicable studies; however, publications that might include relevant data or information on trials will be retained initially. SUN and YIN will independently assess retrieved abstracts and, if necessary, the full text of these studies to determine which trials satisfy the inclusion criteria. Disagreements will be resolved in consultation with JING.

Data extraction and management

Two authors (SUN and ZHANG) will extract the following data from the included randomised trials:

• Trial characteristics: risk of bias, design, number of intervention groups, number of patients with missing data, and length of follow‐up.

• Patient characteristics: number of patients randomised to each intervention group, mean (or median) age, number of males, form and stage of hepatic encephalopathy, mean duration of hepatic encephalopathy at randomisation, type of underlying liver disease, factors precipitating acute hepatic encephalopathy.

• Intervention characteristics: type and dose of experimental and control intervention, duration of therapy, mode of administration, type and dose of additional interventions.

• Outcomes: all outcomes will be extracted from each trial.

Data extraction will be performed independently. Any discrepancies will be resolved by discussion, and if necessary, by referral to a third author (YANG).

Assessment of risk of bias in included studies

SUN and YANG will assess the risk of bias of the trials independently, without masking of the trial names. Any disagreement will be resolved by discussion, and, if necessary, referred to a third author (JING) for adjudication. We will follow the instructions given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008) and the Cochrane Hepato‐Biliary Group Module (Gluud 2008). Due to the risk of biased overestimation of beneficial intervention effects in randomised trials with inadequate methodological quality (Schulz 1995; Moher 1998; Kjaergard 2001; Wood 2008), we will look at the influence of methodological quality of the trials on the results by evaluating the reported:

Generation of the allocation sequence

‐ Adequate, sequence generation was achieved 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 adjudicator.
‐ Unclear, the trial is described as randomised but the method of sequence generation was not specified.
‐ Inadequate, the sequence generation method is not, or may not be, random. Quasi‐randomised studies, those using dates, names, or admittance numbers in order to allocate patients are inadequate and will be excluded for the assessment of benefits but not for harms.

Allocation concealment

‐ Adequate, allocation was controlled by a central and independent randomisation unit, serially numbered, opaque and sealed envelopes or similar, so that intervention allocations could not have been foreseen in advance of, or during, enrolment.
‐ Unclear, the trial was described as randomised but the method used to conceal the allocation was not described, so that intervention allocations may have been foreseen in advance of, or during, enrolment.
‐ Inadequate, if the allocation sequence was known to the investigators who assigned participants or if the study was quasi‐randomised. Quasi‐randomised studies will be excluded for the assessment of benefits but not for harms.

Blinding

‐ Adequate, the trial was described as double blind and the method of blinding was described, so that knowledge of allocation was adequately prevented during the trial.
‐ Unclear, the trial was described as double blind, but the method of blinding was not described, so that knowledge of allocation was possible during the trail.
‐ Not performed, the trial was not double blind, so that the allocation was known during the trail.

Complete outcome data

‐ Adequate, the numbers and reasons for dropouts and withdrawals in all intervention groups were described or if it was specified that there were no dropouts or withdrawals.
‐ Unclear, the report gave the impression that there had been no dropouts or withdrawals, but this was not specifically stated.
‐ Inadequate, the number or reasons for dropouts and withdrawals were not described.

Selective outcome reporting

‐ Adequate, pre‐defined, or clinically relevant and reasonably expected outcomes are reported on.
‐ Unclear, not all pre‐defined, or clinically relevant and reasonably expected outcomes are reported on or are not reported fully, or it is unclear whether data on these outcomes were recorded or not.
‐ Inadequate, one or more clinically relevant and reasonably expected outcomes were not reported on; data on these outcomes were likely to have been recorded.

Other biases

Baseline imbalance
‐ Adequate, if there was no baseline imbalance in important characteristics.
‐ Unclear, if the baseline characteristics were not reported.
‐ Inadequate, if there was an baseline imbalance due to chance or due to imbalanced exclusion after randomisation.

Early stopping
‐ Adequate, if sample size calculations were reported and the trial was not stopped or the trial was stopped early by a formal stopping rule at a point where the likelihood of observing an extreme intervention effect due to chance was low.
‐ Unclear, if sample size calculations were not reported and it is not clear whether the trial was not stopped early or not.
‐ Inadequate, if the trial was stopped early due to an informal stopping rule or the trial was stopped early by a formal stopping rule at a point where the likelihood of observing an extreme intervention effect due to chance.

To report on other bias, one should continue using the following pattern:

‐ Adequate, the trial appears to be free of other components that could put it at risk of bias.
‐ Unclear, the trial may or may not be free of other components that could put it at risk of bias.
‐ Inadequate, there are other factors in the trial that could put it at risk of bias, eg, no sample size calculation made, industry involvement, or an extreme baseline imbalance.

Measures of treatment effect

Statistical analysis will be performed using Review Manager (RevMan 2008) and follow the principles and recommendations set out in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2008) and The Cochrane Hepato‐Biliary Group Module (Gluud 2008). For dichotomous outcomes (eg, patient survival) results will be expressed as relative risk (RR) with 95% confidence intervals (CI) where appropriate. Data will be pooled using the random‐effects model, but the fixed‐effects model will also be analysed to ensure robustness of the model chosen. Where continuous scales of measurement are used to assess the effects of treatment (eg, number of infective episodes), we will use the mean difference (MD); if different scales have been used, then we will use the standardised mean difference (SMD). Paediatric trials will be included and analysed alongside adult trials.

Unit of analysis issues

Non‐standard design randomised clinical trials may present statistical problems in this review. While we do not anticipate cross‐over or cluster randomisation designs, we do expect multiple intervention groups. Care will be taken to avoid 'unit of analysis' errors when analysing these types of trials (Higgins 2008).

Dealing with missing data

Missing data and attrition will be assessed for each of the included trials, and the number of participants who are included in the final analysis will be reported as a proportion of all participants in the trial. Reasons given for missing data will be provided in the narrative summary, and the extent to which the results are altered by missing data will be ascertained. The extent to which trials have conformed to an intention‐to‐treat analysis will also be assessed.

Assessment of heterogeneity

We will use the chi‐squared test to assess heterogeneity between trials and the I² statistic to assess the extent of inconsistency. We will use a fixed‐effect model and a random‐effects model for calculating summary estimates and their 95% confidence intervals (CI). If there is a significant heterogeneity, we will present the results obtained with the both models.

Assessment of reporting biases

Funnel plots will be drawn to investigate any relationship between effect size and study precision (closely related to sample size) (Egger 1997). Such a relationship could be due to publication or related biases, or due to systematic differences between small and large trials. If a relationship is identified, the clinical diversity of the trials will be further examined as a possible explanation and described in the text.

Data synthesis

We will analyse the data using Review Manager (version 5.0) (RevMan 2008) and extract and pool data for summary estimates.

Subgroup analysis and investigation of heterogeneity

In cases where trials and data are available, the following sub‐group analyses will be performed:

• severity of hepatic encephalopathy;

• different doses of naloxone;

• different interventions in the control groups.

Each of these factors has been identified as being important because they may influence a person's inclination or opportunity to engage with, and benefit from, interventions.

Sensitivity analysis

Missing data will be dealt with according to the strategy outlined above; however, as part of the data analysis 'poor', 'good' and 'extreme case' analyses will also be conducted to assess the robustness of the findings. A summary table will be produced detailing decisions made during the process of conducting the review and the potential impact of these decisions on findings. Significant decisions will be addressed in the Discussion section.

Regarding the primary outcome measure, we will include patients with incomplete or missing data in sensitivity analyses by analysing them according to the principles of intention‐to‐treat. Furthermore, we will do extreme case analyses where dropouts are considered as failures in the experimental group and as success in the control group, and vice versa. The following scenarios will be considered to ensure robustness of the data:

‐ Carry forward analysis: if patients have missing outcome data, we will use the last reported observed response ('carry forward') in the nominator and will include all randomised participants in the denominator.

‐ Poor outcome analysis: assuming that dropouts or participants lost from both the experimental and control groups had the primary outcome including all randomised participants in the denominator.

‐ Good outcome analysis: assuming that none of the dropouts or participants lost from the experimental and control groups had the primary outcome including all randomised participants in the denominator.

‐ Extreme case favouring the experimental intervention: none of the dropouts or participants was lost from the experimental group, but all dropouts or participants that were lost from the control group had the primary outcome including all randomised participants in the denominator.

‐ Extreme case analysis favouring control: all dropouts or participants lost from the experimental group, but none from the control group had the primary outcomes including all randomised participants in the denominator.