Machine perfusion in liver transplantation: a network meta‐analysis

Objectives

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

To perform pairwise comparisons and network meta‐analyses to assess the effects of static cold storage and different methods of machine perfusion (including hypothermic oxygenated machine perfusion, normothermic machine perfusion, controlled oxygenated rewarming, and normothermic regional perfusion) in people undergoing liver transplantation.

Background

Description of the condition

Liver transplantation is the only definitive treatment for end‐stage liver disease. Continuous advances in transplant medicine have resulted in excellent outcomes during recent years; the average five‐year post liver transplantation survival is now around 80% in adults in the UK and USA (NHSBT 2019; Kwong 2020). However, the lack of available organs results in significant mortality for those on the waiting list (NHSBT 2019; Kwong 2020). In addition, many people who could receive a life‐saving transplant do not meet current inclusion criteria, as the precious and sparse resource of human organs is carefully allocated.

Currently, approximately one‐third of retrieved organs in the UK do not proceed to transplant (NHSBT 2019). Optimal liver grafts are donated following brainstem death (where warm ischaemic time is low) from standard criteria donors, who are younger than 50 years old, without hepatic steatosis or viral hepatitis (Saidi 2013). Recent attempts to expand the donor pool have resulted in the increasing use of sub‐optimal organs from expanded criteria donors, who are elderly, have hepatic steatosis, malignancies, or viral hepatitis, and those who donated following circulatory death (Saidi 2013). However, it is well documented that these grafts have worse outcomes (both short‐term graft function and long‐term graft survival) if additional measures are not taken to improve preservation and optimise function (Briceño 2009; Foley 2011; Laing 2016; Nemes 2016). Machine perfusion of the donor liver may preserve a donor liver better than static cold storage.

Machine perfusion was first described nearly a century ago (Dutkowski 2008). There has been a resurgence of interest during the last twenty years, in the hope that machine perfusion could better preserve and optimise sub‐optimal grafts, thereby, improving graft and recipient survival following transplantation. Machine perfusion could also potentially allow some of the poorer quality retrieved livers, which currently are not used for transplantation, to be used, further expanding the donor pool (NHSBT 2019).

Description of the intervention

It has long been known that reducing the temperature of organs can prolong their preservation time (Collins 1969). Clinically, this is achieved using a preservation solution to perfuse and surround the liver, which is then packaged in an ice box (termed static cold storage). This is a satisfactory method for preserving high‐quality liver grafts, which are reasonably resistant to ischaemia reperfusion injury. However, as the number of donors with expanded criteria, and the number of organ donations after cardiac death have risen to try and match the demand for donor organs, there has been increased interest in alternative preservation methods, which may prove superior to standard static cold storage (NHSBT 2019; Kwong 2020).

Several machine perfusion technologies have been developed, which aim to improve organ preservation between donor and recipient, and optimise high‐risk grafts. These include normothermic machine perfusion (NMP), hypothermic oxygenated machine perfusion, controlled oxygenated rewarming, and normothermic regional perfusion (Dutkowski 2014; Oniscu 2014; Dutkowski 2015; Guarrera 2015; Hoyer 2016; Nasralla 2018; Hessheimer 2019). The basic components of all of these perfusion circuits are a membrane oxygenator to deliver oxygen and remove CO₂, a pump (which can provide continuous or pulsatile flow), a heater‐cooler unit, a reservoir, and infusion pumps.

A detailed description of every proposed machine perfusion protocol is outside the scope of this current Cochrane Review, but has been recently reviewed (Czigany 2019). Perfusion can be done in the donor, during transportation of the organ from donor to recipient, or prior to implantation at the recipient hospital (end‐ischaemic). Some perfusions are normothermic, and some are hypothermic, but the exact target temperature used in different protocols varies. Hypothermic techniques can be completed without an oxygen carrier, whereas normothermic techniques require an oxygen carrier, which is often, but not always, human red blood cells (Matton 2018).

Evidence from the kidney transplantation literature provides hope that machine perfusion may be able to improve clinical outcomes (Tingle 2019). In deceased donor renal transplantation, non‐oxygenated hypothermic machine perfusion (during transport) improved early function, and increased long‐term graft survival in organs procured after brain death (DBD), and after cardiac death (DCD), when compared to static cold storage (Tingle 2019).

How the intervention might work

Traditional static cold storage aims to preserve transplant organs by lowering their metabolic rate. In general, for every 10 °C drop, the metabolism rate is halved (Wilson 2006). Therefore, at 4 °C, the enzymatic rate is approximately 10% of that at 37 °C (Wilson 2006). Static cold storage works by removing blood and clots from the liver graft, and replacing them with an acellular preservation solution in a hypothermic environment. However, in this oxygen depletion system, metabolism does not completely halve. This results in adenosine triphosphate (ATP) depletion and ischaemic injury ensues, priming the graft for further reperfusion injury (Martin 2019).

Hypothermic oxygenated machine perfusion uses commercially available machines to deliver oxygenated perfusate while maintaining the principle of lowering metabolic activity through hypothermia. Protocols in current use describe end‐ischaemic hypothermic oxygenated machine perfusion in the recipient hospital (Dutkowski 2014; Dutkowski 2015; Guarrera 2015; van Rijn 2018).

There are multiple proposed beneficial effects of performing hypothermic oxygenated machine perfusion. First, there is a physical washout benefit that helps to clear the microcirculation in the liver, which includes diluting waste products and blood remnants. The Porte Group, from the Netherlands, demonstrated that hypothermic oxygenated machine perfusion increased ATP content more than 15‐fold, which remained elevated after reperfusion (Westerkamp 2016; van Rijn 2017). There also appears to be reduced expression of pro‐inflammatory cytokines (Schlegel 2014a), downregulation of Kupffer cell activity (Guarrera 2011; Schlegel 2013a), and reduced vascular resistance (Lee 2002; Op den Dries 2014). The delivery of oxygen, and recovery of mitochondria before restoration of normothermia (which is not achieved by normothermic machine perfusion), is thought to be critical in preventing reperfusion injury (Schlegel 2013b; Schlegel 2014b).

Normothermic machine perfusion aims to maintain physiological conditions and a metabolically active liver by providing oxygen and nutrients. Normothermic machine perfusion replenishes liver ATP, and allows reperfusion to take place in a controlled environment, isolated from the recipient's immune and coagulation systems (Brockmann 2009; Xu 2012). Normothermic machine perfusion can be performed in transit, therefore, avoiding ATP depletion and loss of metabolic homeostasis, which occurs with prolonged static cold storage (Nasralla 2018; Martin 2019). Finally, as normothermic machine perfusion maintains a metabolically active organ, theoretically, it has benefits over hypothermic perfusion as a tool for viability assessment, and therefore, it could improve organ utilisation (Mergental 2016; Watson 2018).

Controlled oxygenated rewarming aims to capitalise on the aforementioned benefits of both hypothermic oxygenated machine perfusion and normothermic machine perfusion, including early mitochondrial recovery and viability testing (von Horn 2017). Another key factor is the concept of rewarming injury. In animal models, the process of rapid rewarming (and resulting rapid increase in metabolic demands) has been shown to be detrimental (Minor 2019). In theory, controlled oxygenated rewarming allows early recovery of mitochondria, avoidance of rewarming injury, and maintenance of a metabolically active organ for prolonged preservation and viability testing.

Normothermic regional perfusion in the donor is an alternative approach. Cannulae are placed to access the subdiaphragmatic aorta and inferior vena cava, and oxygenated blood is circulated through abdominal organs while they remain in situ. Animal models have shown that normothermic regional perfusion replenishes ATP and improves anti‐oxidant levels (Net 2001; Net 2005). Legislation in some countries allows cannulation and heparinisation of potential DCD donors pre‐mortem; in this setting, normothermic regional perfusion can greatly reduce warm ischaemic time (Hessheimer 2019). This is the only technique that is performed prior to in situ cold flush. Breaking the chain between peri‐mortem warm ischaemia and cold ischaemia may lead to improved outcomes.

Why it is important to do this review

Several machine perfusion technologies have been developed which aim to improve utilisation and outcomes of donated livers. Furthermore, improved techniques, which allow prolonged preservation, could have logistical benefits and allow a shift towards operating in daylight hours.

Despite promising clinical data, it is unclear if machine perfusion functions better than static cold storage. It remains unclear which of these perfusion methods, and which perfusion protocols, result in the best clinical outcomes for the various types of available grafts. Trials often compare a new perfusion technique with standard static cold storage, with a lack of head‐to‐head comparisons among perfusion protocols. The use of network meta‐analysis would help to answer these questions. To our knowledge, there are no previous systematic reviews or (network) meta‐analyses of randomised controlled trials in liver machine perfusion.

It is vital to analyse the data from randomised trials to identify the impact of machine perfusion, and to compare different perfusion strategies, to establish the role of these techniques in clinical practice.

Objectives

To perform pairwise comparisons and network meta‐analyses to assess the effects of static cold storage and different methods of machine perfusion (including hypothermic oxygenated machine perfusion, normothermic machine perfusion, controlled oxygenated rewarming, and normothermic regional perfusion) in people undergoing liver transplantation.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised clinical trials that compare preservation methods in deceased donor liver transplantation, if at least one intervention group uses machine perfusion. We anticipate that some trials will randomise at the recipient level, whereas some trials will randomise the liver graft into an intervention group (especially those techniques where perfusion is initiated at the donor hospital). We will include both kinds of trials. We will only use quasi‐randomised studies, in which allocation to treatment was obtained by alternation, use of alternate medical records, date of birth, or other predictable methods, and observational studies for the report on harms (in a narrative way), but will not include their information to our main meta‐analyses.

Types of participants

Inclusion criteria

Recipients of whole, deceased donor liver transplants from donors following either cardiac (DCD) or brain death (DBD). We will include studies that include recipients of donors who met both standard criteria and expanded criteria for donors (Saidi 2013). All adult recipients of liver transplants are eligible, including those receiving a retransplant. We will include trials investigating liver utilisation proportions, which randomise liver grafts to a perfusion group; in this setting, the participant is the randomised donor liver. We will include trials where only a subset of the participants are eligible; we will only use data from these trials for quantitative synthesis if effect estimates are available for the subset of eligible participants (either in published work, or via contact with study authors). We will only include trials in humans.

Exclusion criteria

We will exclude any studies with unethical retrieval of livers (ISTTOT 2008). Therefore, we will assess whether publications identified in our searches have since been withdrawn, due to fraud or unethical organ retrievals. We will exclude case series comparing perfusion techniques to retrospective cohorts. We will exclude grafts that have been split or reduced, or used as part of a multivisceral transplant. We will exclude pre‐clinical studies investigating machine perfusion technologies where none of the grafts proceeded to transplant.

Types of interventions

Several machine perfusion technologies have been described, and any of these are eligible for inclusion. Specifically, we plan to have the following nodes in our network meta‐analysis: static cold storage (control), hypothermic oxygenated machine perfusion, normothermic machine perfusion, controlled oxygenated rewarming, or normothermic regional perfusion. We expect that in the future, some trials may combine these techniques (for example, normothermic regional perfusion followed by normothermic machine perfusion). We will include all of these interventions, as well as static cold storage (the current standard of care) in the decision set.

Types of outcome measures

We will assess outcomes at the maximum follow‐up, unless stated otherwise, for each of the following outcomes.

Primary outcomes

• Overall participant survival

• Quality of life, assessed using any validated scale

• Serious adverse events. We will accept individual complications and serious adverse events defined by:

  • Clavien‐Dindo classification, grade III or higher (Dindo 2004; Clavien 2009);

  • International Conference on Harmonization–Good Clinical Practice (ICH‐GCP) guideline: any untoward medical occurrences that result in death, are life threatening, require inpatient hospitalisation or prolongation of existing hospitalisation, and result in persistent or significant disability or incapacity (ICH‐GCP 1997).

Secondary outcomes

• Graft survival

• Ischaemic biliary complications, within six months and at maximum follow‐up (e.g. ischaemic‐type biliary lesions (Foley 2011))

• Primary non‐function of the graft

• Early allograft function, measured with a validated model (seven days) (e.g. Early Allograft Dysfunction or Model for Early Allograft Funtion criteria (Olthoff 2010; Pareja 2015; Jochmans 2017))

• Adverse events not considered serious by the aforementioned definitions

• Transplant utilisation (proportion of grafts allocated to an intervention that proceed to transplant)

• Transaminase release during the first week post‐transplant (participant serum) (until seven days)

We will not draw conclusions on the superiority of a perfusion technique based solely on outcomes such as early allograft dysfunction and transaminase release post‐transplant. These outcomes are included as they are all either markers of the degree of reperfusion injury, or have been used as surrogate markers of graft survival in large trials (Nasralla 2018). Some scientists consider them to be important in the field of liver machine perfusion when trials powered for overall participant survival or graft survival are difficult to conduct.

Neither will we draw conclusions on the superiority of a technique based on graft utilisation, taken in isolation. We will always consider graft utilisation in the context of the outcomes in grafts that are transplanted. If a certain preservation technique increases graft utilisation while improving, or maintaining recipient outcomes, this is clearly of benefit. However, if a trial randomising grafts to a preservation technique shows that one technique improves utilisation, but the recipient outcomes in this group are worse, we cannot know whether this increased utilisation was beneficial; only a cluster‐randomised trial of survival in people on the waiting list could answer this question. Further discussion of these issues is found in our Unit of analysis issues section.

Outcomes for ranking in network meta‐analysis

We plan to rank the interventions based on their effects on our primary outcomes plus the outcomes: graft survival, ischaemic‐type biliary complications, and adverse events considered non‐serious.

Search methods for identification of studies

Electronic searches

We will search the Cochrane Hepato‐Biliary Group Controlled Trials Register (maintained and searched internally by the Cochrane Hepato‐Biliary Group Information Specialist via the Cochrane Register of Studies Web), Cochrane Central Register of Controlled Trials (CENTRAL; latest issue), MEDLINE Ovid (1946 to present), Embase Ovid (1974 to present), LILACS (Bireme; 1982 to present); Science Citation Index Expanded (Web of Science; 1900 to present); and Conference Proceedings Citation Index (Web of Science; 1990 to present). Appendix 1 gives the preliminary search strategies with the expected time spans of the searches.

We will also search the following on‐line trial registries to identify ongoing and unpublished trials: ClinicalTrial.gov (clinicaltrials.gov/), European Medicines Agency (EMA; www.ema.europa.eu/ema/), WHO International Clinical Trial Registry Platform (ictrptest.azurewebsites.net/Default.aspx), and the Food and Drug Administration (FDA; www.fda.gov).

Searching other resources

We will search the reference lists of relevant studies and clinical practice guidelines. We will also search the reference lists of recent reviews on liver machine perfusion (for example Czigany 2019 and Schlegel 2019).

Data collection and analysis

We will perform this review in line with recommendations from the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021a).

Selection of studies

Two review authors, ST and ET, will independently screen titles identified by our search strategy. They will discard reports that do not fulfil the inclusion criteria of this review; however initially, we will retain reports of studies and reviews that may include relevant data or references to relevant trials. ST and ET will then independently assess retrieved abstracts, and if necessary, the full text of these studies to determine which studies satisfy the inclusion criteria. CW will resolve any differences in opinion.

If multiple publications exist for a single randomised trial, we will list all of them under a single, main study reference. We also plan to include studies that are only available as conference abstracts. We will include trials in the review, regardless of whether measured outcome data are reported in a usable way, only if we can ensure that these studies were not withdrawn because of ethical or other reasons. We will include studies that fulfil our inclusion criteria, even if they do not measure any of our outcomes of interest. We will generate a PRISMA flowchart to detail the output of our search and study selection (Liberati 2008).

Data extraction and management

ST and ET will independently extract necessary data from included trials, using a pre‐piloted data extraction form. This will include information on trial characteristics, included participants, type(s) of machine perfusion, additional potential effect modifiers, outcome data (including measurement time point), and source of funding. We will resolve any discrepancies with the senior author, CW.

Assessment of risk of bias in included studies

ST and ET will independently assess risk of bias, and if differences of opinion arise, CW will arbitrate. We will use RoB 2, as outlined in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021b).

We will assess the effect of assignment to the intervention, using RoB 2 (Higgins 2021b). Therefore, we will perform analysis based on the intention‐to‐treat (ITT) principle, which includes all randomised participants, regardless of the interventions that participants actually received.

In brief, we will assess the following sources of bias in the individually randomised trials, at the outcome level, using RoB 2 (Sterne 2019; Higgins 2021b).

• Bias arising from the randomisation process

• Bias due to deviations from intended interventions

• Bias due to missing outcome data

• Bias in measurement of the outcome

• Bias in selection of the reported result

As per the Cochrane Handbook for Systematic Reviews of Interventions guidance, we will use RoB 2 to assess the risk of bias for only a subset of outcomes (Higgins 2021b). There is currently a lack of guidance on how to select outcomes for which to perform risk of bias assessments; we will select outcomes based on the most contemporaneous advice from Cochrane. The risk of bias assessments feed into one domain of the GRADE approach for assessing certainty of a body of evidence (Schünemann 2021a). For the risk of bias assessment, we will focus on results of the trials that contribute information that users of the review will find most useful; overall participant survival at maximum follow‐up, quality of life, serious adverse events, graft survival, ischaemic biliary complications (ischaemic‐type biliary lesions) within one year, and adverse events considered non‐serious.

We will carefully study the latest (i.e. at the time of review production) guidance on preliminary consideration for assessing risk of bias, the signalling questions to be used, and the response options for the signalling questions, such as yes, probably yes, no, probably no, and no information (Sterne 2019; Higgins 2021b). We will use the most recently developed RoB2 Excel tool. An algorithm in Excel maps the responses to the signalling questions per outcome, and proposes a risk of bias judgement for each domain. We will store the Excel spreadsheets for each trial outcome on a secure server, which will be available upon request.

Overall risk of bias

The overall rating assigns one of three levels of judgement:

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

We will use the same levels of overall risk of bias judgements across different trials for each of the domains listed as we used for the individual domains, that is 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 follow the guidance on preliminary consideration for assessing risk of bias on how to record risk of bias in trial data obtained through different sources, e.g. unpublished data, correspondence with a trialist, etc.

Measures of treatment effect

We will use odds ratios (OR) with 95% confidence intervals (CI) for dichotomous outcomes, and mean difference (MD) with 95% CI for continuous data. We plan to analyse graft and participant survival as time‐to‐event data, and perform meta‐analysis using the general inverse‐variance method, as described in chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2021). This may require extraction of O ‐ E and V (observed minus expected and variance) statistics to calculate hazard ratios. If data in included trials are insufficient to allow extraction of O ‐ E and V statistics, we may need to analyse survival as a dichotomous variable at set time points (one, three, and five years). In this instance, we will use one‐year graft survival as a primary outcome.

In the event that multiple studies report on quality of life using different measures, we will pool the results using standardised mean difference (SMD) with 95% CI. We will then express this standardised mean difference in the units of whichever quality of life instrument is used by the largest number of studies. This will be done by multiplying the standardised mean difference by a weighted standard deviation, calculated using the standard deviation from all studies using that instrument. This is described further in Chapter 15.5.3.2 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2021b).

Unit of analysis issues

We anticipate that included trials will randomise either at the level of the transplant recipient or at the level of the liver graft. For trials randomising transplant recipients, we do not foresee any unit of analysis issues. Studies randomising liver grafts may report on graft utilisation; for this outcome, the unit of analysis will be the liver grafts. Such trials are likely to report on recipient outcomes; in this case, the unit of analysis will be the transplant recipient. We do not expect cluster or cross‐over trails. We will analyse the results using intention‐to‐treat analysis wherever possible.

If any trials are identified with more than two treatment arms, we will attempt to incorporate these into network meta‐analyses. For pair‐wise analyses using such trials, we will either omit irrelevant groups or combine multiple arms, as outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021a).

Dealing with missing data

Our preferred method of dealing with missing data is to contact study authors and attempt to obtain missing data from them directly. When this fails, we will attempt to impute missing data using methods outlined in the Cochrane Handbook for Systematic Reviews of Interventions (e.g. last observation carried forward; imputing an assumed outcome, such as assuming all were poor outcomes; imputing the mean; imputing based on predicted values from a regression analysis (Higgins 2021a)). Selection of imputation method will depend on the data available; if multiple methods are appropriate, we will perform sensitivity analyses with each.

For missing standard deviations, we will attempt to impute these from P values, 95% CIs, or from other studies with similar designs, participant groups, and numbers (Furukawa 2006). As described above, we will attempt to analyse survival as time‐to‐event data. This may require imputation from hazard ratios, P values, 95% CIs, etc. In all cases of imputed data, we will perform a sensitivity analysis to assess how sensitive these assumptions are to reasonable changes and variance.

Assessment of heterogeneity

Pairwise meta‐analysis

First, we will visually assess heterogeneity, using forest plots generated from pairwise comparison meta‐analyses. We will pay particular attention to the following potential effect modifiers when assessing heterogeneity: DCD compared to DBD, expanded criteria donors compared to standard criteria donors, steatotic grafts, age of donors, duration of cold ischaemic time or perfusion time, type of perfusion fluid used, and recipient factors (age, indication, retransplant).

Then, we will analyse the presence and extent of heterogeneity using the standard I² statistic (the percentage of the variability in effect estimates that is due to heterogeneity rather than chance). Strict cut‐offs for I² are often not useful, especially when the number of trials is low (making the Chi² test, which underlies the I² statistic, underpowered). However, we will use the following thresholds as a guide (Higgins 2021a):

• 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.

Network meta‐analysis

We will generate tables that will allow us to evaluate the distribution of the effect modifiers, listed above, across different comparisons, and therefore, assess the validity of the transitivity assumption for indirect comparisons (see Data synthesis below). For information on how we will statistically analyse whether the transitivity assumption has been violated, see 'Inconsistency in network meta‐analysis', below (Data synthesis).

Assessment of reporting biases

We will use funnel plots to allow a visual assessment of the presence of publication bias if there are at least 10 trials in the analysis (Higgins 2021a). For network meta‐analysis, we will construct comparison‐adjusted funnel plots (Ratnayake 2019).

Data synthesis

We will perform all data analyses following instructions from the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021a). For pairwise analyses, we will use Review Manager 5 (Review Manager 2020) and RevMan Web (Review Manager Web). We will perform network meta‐analyses in R using the GeMTC package (R 2021; Valkenhoef 2016). If meta‐analysis is not possible, we will use alternative methodologies to report results. Our approach will be guided by risk of bias and completeness of the available data, but may include: summarising effect estimates, using box‐and‐whisker plots; vote counting, based on direction of effect; and structured tabulation of results across studies.

Pairwise meta‐analysis

We will perform individual pairwise meta‐analyses when there is direct evidence from at least two trials comparing the same preservation techniques. We will perform this using random‐effects models for our main analyses.

Network meta‐analysis

We will perform network meta‐analyses using the GeMTC user interface (Valkenhoef 2016). This interface is powered by the GeMTC R package, which performs network meta‐analysis using a Bayesian hierarchical model (Valkenhoef 2016). We will use Markov Chain Monte Carlo (MCMC) methods to sample the posterior distribution. A key benefit of the GeMTC package is the ability to automate Bayesian hierarchical model generation, which includes the use of the supplied dataset to heuristically set priors that limit bias, and starting values that limit the chance of misdiagnosing convergence (Valkenhoef 2012).

Priors will be vague (non‐informative) and will be generated heuristically, based on the data provided by the included clinical trials. These priors will be sufficiently vague (large variance), such that posteriors (model results) are dominated by data provided by included trials, rather than the chosen prior distributions.

For each model, we will assess convergence visually. By using the Brooks–Gelman–Rubin diagnostic, we will run the model several times in parallel, with different starting values (overdispersed starting values are automatically generated, based on the dataset, such that the parameter space is sufficiently explored); each of these chains will then be compared, generating the potential scale reduction factor (PSRF). We will use a cut‐off PSRF < 1.05, along with visual assessments of PSRF plots and time series plots, to represent acceptable convergence. By default, GeMTC sets burn in (the number of initial MCMC iterations that are discarded) at 5000, and the inference iterations (the following MCMC iterations that are actually used to draw inferences on the posterior distributions) at 20,000, We will adjust these default values as necessary, based on PSRF values, PSRF plots, and time series plots.

Once we have ensured convergence, we will assess how well the model fits the trial data. The key measure of model fit, which we will use, is the residual deviance. We will analyse both overall model fit and per‐treatment arm residual deviance, with values close to 1 representing good model fit.

Further technical details regarding the GeMTC package are available in a peer‐reviewed manuscript (Valkenhoef 2012); further details of the GeMTC user interface are available in the user manual (Valkenhoef 2016).

We will use an intention‐to‐treat principle, and we will derive mean estimates where necessary. We will generate network maps (diagrammes) for each outcome for which network meta‐analyses can be performed. We will generate forest plots to display the results of the network meta‐analyses as a series of pairwise comparisons. The network meta‐analyses output will comprise odd ratios for dichotomous data and mean differences for continuous data, accompanied by 95% credible intervals (CrI). We will then generate ranking summary tables and rankograms with 95% CrI, which will provide the probability of each intervention being ranked in a certain position (first, second, etc) for each outcome.

Transitivity is a key assumption of network meta‐analysis. This is the assumption that effect modifiers (such as donor and recipient characteristics) are similar in all included trials (Salanti 2012). This means that any participant could theoretically have been randomised to any of the treatment options (termed joint randomisability). Transitivity also requires that treatments grouped into a single node are sufficiently similar. As described above, we will consider the following potential effect modifiers when evaluating transitivity: DCD versus DBD, expanded criteria versus standard criteria donors, steatotic grafts, age of donors, duration of cold ischaemic time or perfusion time, type of perfusion fluid used, and recipient factors (age, indication, retransplants). To achieve a connected network, we foresee having to group the static cold storage arms of multiple trials into a single node, even though different cold storage solutions may be used.

Incoherence in network meta‐analysis

Measures of incoherence (sometimes referred to as inconsistency) allow statistical testing to determine whether the transitivity assumption has been violated. The null hypothesis for these analyses is that the network displays transitivity. It may not be possible to perform statistical tests of incoherence, as we predict all trials will have two arms and use static cold storage as their control arm. Therefore, networks will not have any complete loops (a star network), and we will not be able to compare treatment effects calculated from different loops.

If we are able to perform incoherence testing, we will test for global incoherence in the entire network, as well as analysing local incoherence, by comparing indirect with direct effect estimates (also referred to as the node‐splitting method). We will follow methodology described by Dias and colleagues, and outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Dias 2010; Higgins 2021a).

Subgroup analysis and investigation of heterogeneity

We plan to perform the following subgroup analyses, if sufficient data are present:

• Trials at overall low risk of bias compared to trials with some concerns, and trials at high risk of bias, as trials with some concern and at high risk of bias may overestimate or underestimate the intervention effects (Higgins 2021b)

• Trials without for‐profit funding compared to trials with some concern or at risk of for‐profit funding, as conflicts of interest can introduce bias, including publication bias (Lundh 2017)

• Donation following circulatory death (stratified by Maastricht criteria) compared to donation following brainstem death, as these grafts have different patterns of ischaemic injury, and therefore, treatment effects may vary (Thuong 2016)

• Standard criteria donors compared to extended criteria donors, as standard criteria organs may be more resilient to ischaemia reperfusion injury, meaning preservation effects may vary

• Continuous perfusion during transport compared to perfusion at the recipient centre (end‐ischaemic), as the prior cold ischaemic time in the latter group may alter treatement effect size

We will assess statistical heterogeneity as described above. We will perform this assessment for the overall cohort, and within each subgroup, providing insights into the source of any heterogeneity present.

Sensitivity analysis

We plan to assess the sensitivity of our results to changes in methodology, by performing the following sensitivity analyses of our outcome measures:

• Fixed‐effect model (for pairwise meta‐analyses)

• Including only trials at low risk of bias

• Analyses excluding trials for which we imputed data

• We will compare our assessments of imprecision with Trial Sequential Analysis (Castellini 2018; Gartlehner 2019; Jakobsen 2014) with that of GRADE for the outcomes in the summary of findings tables; i.e. proportion of participant survival at maximum follow‐up, quality of life, serious adverse events, graft survival, ischaemic biliary complications (ischaemic‐type biliary lesions) within one year, and adverse events considered non‐serious.

Trial Sequential Analysis

Trial Sequential Analysis considers the choice of statistical model (fixed‐effect or random‐effects meta‐analysis) and diversity (TSA 2017; Thorlund 2017). 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; Brok 2009; Thorlund 2010; Wetterslev 2008; 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 trials according to the year of publication, and if more than one trial was published in a year, we will add trials alphabetically according to the last name of the first author. On the basis of the DARIS, we will construct the trial sequential monitoring boundaries for benefit, harm, and futility (Thorlund 2017; Wetterslev 2008; Wetterslev 2009; Wetterslev 2017). These boundaries 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 may be established, and further trials may be superfluous. If the boundaries for benefit or harm 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 additional trials may be needed.

In our Trial Sequential Analysis of the two primary dichotomous outcomes, we will base the DARIS on event proportions in the control group, assuming a plausible RRR for all‐cause mortality of 20%, and serious adverse events of 20%; risk of type I error of 2.5% due to the three primary outcomes (Jakobsen 2014); risk of type II error of 10% (power 90%); and the diversity of trials included in the meta‐analysis. For the continuous outcome, health‐related quality of life, we plan to estimate the DARIS using a minimal relevant difference of the standard deviation/2; type I error risk of 2.5% due to the three primary outcomes (Jakobsen 2014); risk of type II error of 10% (power 90%); and diversity, as estimated from trials in the meta‐analysis (Wetterslev 2009). We will also calculate Trial Sequential Analysis–adjusted CIs (Thorlund 2017; Wetterslev 2017).

In our Trial Sequential Analysis of secondary outcomes, we will base the DARIS for dichotomous outcomes on the event proportion in the control group; we will make an assumption of an RRR of 20% for graft survival; ischaemic biliary complications; early allograft function; and adverse events not considered serious; type I error risk of 2.0% due to the four secondary outcomes (Jakobsen 2014); risk of type II error of 10% (power 90%); and the diversity of trials included in the meta‐analysis. For continuous outcomes, please see above.

In our Trial Sequential Analysis, we will downgrade our assessment of imprecision by two levels if the accrued number of participants is below 50% of the DARIS, and one level if between 50% and 100% of DARIS. We will not downgrade if futility or DARIS is reached, or crossed by the cumulative Z score.

A more detailed description of Trial Sequential Analysis and the software programme can be found at www.ctu.dk/tsa/ (Thorlund 2017).

For any continuous data on survival, we may consider adopting the methodology by Miladinovic and colleagues to control random errors (Miladinovic 2013; Miladinovic 2013a; Miladinovic 2013b) using parameters similar to above.

Sensitivity analyses in the network meta‐analysis

For the network meta‐analyses, we will undertake a sensitivity analysis by sequentially removing single trials to review the resulting discrepancies in the ranking data.

Summary of findings and assessment of the certainty of the evidence

We will create a summary of findings table using the following outcomes: overall participant survival at maximum follow‐up, quality of life, serious adverse events, graft survival, ischaemic biliary complications (within six months), early allograft dysfunction (seven days), and adverse events considered non‐serious. We will include these in the summary of findings tables even if no data are available for these outcomes. We will use the five GRADE domains i.e. risk of bias (we will use the overall RoB 2 judgement), inconsistency, imprecision, indirectness, and publication bias to assess the certainty of evidence as it relates to the trials that contribute data for the prespecified outcomes (Schünemann 2013). We will use the methods and recommendations described in Chapter 14 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2021a), using GRADEpro GDT software (GRADEpro GDT). We will justify all decisions to downgrade the certainty of evidence using footnotes, and we will make comments to aid the reader’s understanding of the review where necessary.

We will assess the certainty of evidence as falling into one of these levels 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.

Two authors will independently assess the certainty of evidence (ST and ET), and disagreements will be resolved by a third review author (CW). Next to each outcome in the summary of findings table, we will also provide the duration of the analysed follow‐up data (including its mean and range).

Network meta‐analysis

We will assess the confidence in outputs from the network meta‐analyses (certainty of evidence) using the CINeMA (Confidence In Network Meta‐Analysis) online tool (Salanti 2014; CINeMA 2017). We will assess the confidence in each individual comparison by considering the following six domains: within‐study bias, indirectness, imprecision, heterogeneity, incoherence, and reporting bias. This will allow us to generate summary tables on the confidence in the results from each individual comparison in the network meta‐analyses. We will generate summary of findings tables for network meta‐analyses using the approach detailed by Yepes‐Nuñez 2019.

Appendices

Appendix 1. Appendix 1. Search Strategies

Database	Time span	Search strategy
Cochrane Hepato‐Biliary Group Controlled Trials Register	Date will be given at review stage	(((organ* or machine* or regional*) and (perfusion* or preservation*)) or oxygenated rewarming or static cold storage) and ((liver or hepat*) and (transplant* or graft*))
Cochrane Central Register of Controlled Trials	Latest issue	#1 MeSH descriptor: [Perfusion] explode all trees #2 MeSH descriptor: [Organ Preservation] explode all trees #3 (((organ* or machine* or regional*) near (perfusion* or preservation*)) or oxygenated rewarming or static cold storage) #4 #1 or #2 or #3 #5 MeSH descriptor: [Liver Transplantation] explode all trees #6 ((liver or hepat*) and (transplant* or graft*)) #7 #5 or #6 #8 #4 and #7
MEDLINE Ovid	1946 to the date of the search	1. exp Perfusion/ 2. exp Organ Preservation/ 3. (((organ* or machine* or regional*) adj (perfusion* or preservation*)) or oxygenated rewarming or static cold storage).mp. [mp=title, abstract, original title, name of substance word, subject heading word, floating sub‐heading word, keyword heading word, organism supplementary concept word, protocol supplementary concept word, rare disease supplementary concept word, unique identifier, synonyms] 4. 1 or 2 or 3 5. exp Liver Transplantation/ 6. ((liver or hepat*) and (transplant* or graft*)).mp. [mp=title, abstract, original title, name of substance word, subject heading word, floating sub‐heading word, keyword heading word, organism supplementary concept word, protocol supplementary concept word, rare disease supplementary concept word, unique identifier, synonyms] 7. 5 or 6 8. 4 and 7 9. (random* or blind* or placebo* or meta‐analys*).mp. [mp=title, abstract, original title, name of substance word, subject heading word, floating sub‐heading word, keyword heading word, organism supplementary concept word, protocol supplementary concept word, rare disease supplementary concept word, unique identifier, synonyms] 10. 8 and 9
Embase Ovid	1974 to the date of the search	1. exp perfusion/ 2. exp organ preservation/ 3. (((organ* or machine* or regional*) adj (perfusion* or preservation*)) or oxygenated rewarming or static cold storage).mp. [mp=title, abstract, heading word, drug trade name, original title, device manufacturer, drug manufacturer, device trade name, keyword, floating subheading word, candidate term word 4. 1 or 2 or 3 5. exp liver transplantation/ 6. ((liver or hepat*) and (transplant* or graft*)).mp. [mp=title, abstract, heading word, drug trade name, original title, device manufacturer, drug manufacturer, device trade name, keyword, floating subheading word, candidate term word] 7. 5 or 6 8. 4 and 7 9. (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 word, candidate term word] 10. 8 and 9
LILACS BIREME	1982 to the date of the search	(((organ$ or machine$ or regional$) and (perfusion$ or preservation$)) or oxygenated rewarming or static cold storage) [Words] and ((liver or hepat$) and (transplant$ or graft$)) [Words]
Science Citation Index Expanded (Web of Science)	1900 to the date of the search	#5 #4 AND #3 #4 TS=(random* or blind* or placebo* or meta‐analys*) #3 #2 AND #1 #2 TS=((liver or hepat*) and (transplant* or graft*)) #1 TS=(((organ* or machine* or regional*) near (perfusion* or preservation*)) or oxygenated rewarming or static cold storage)
Conference Proceedings Citation Index – Science (Web of Science)	1990 to the date of the search	#5 #4 AND #3 #4 TS=(random* or blind* or placebo* or meta‐analys*) #3 #2 AND #1 #2 TS=((liver or hepat*) and (transplant* or graft*)) #1 TS=(((organ* or machine* or regional*) near (perfusion* or preservation*)) or oxygenated rewarming or static cold storage)

Appendix 2. Descriptions of the bias domains in RoB 2 tool for randomised trials with a summary of the issues addressed

Bias domain	Issues addressed
Risk of bias arising from the randomisation process	Was the allocation sequence random? Was the allocation sequence concealed until participants were enrolled and assigned to interventions? Did baseline differences between intervention groups suggest a problem with the randomisation process?
Risk of bias due to deviation from the intended intervention (effect of assignment to intervention)	Whether: participants were aware of their assigned intervention during the trial; carers and people delivering the interventions were aware of participants' assigned intervention during the trial. When interest is in the effect of assignment to intervention: (if applicable) deviations from the intended intervention arose because of the experimental context, and if so, whether they were unbalanced between groups and likely to have affected the outcome; an appropriate analysis was used to estimate the effect of assignment to intervention.
Bias due to missing outcome data	Whether: data for this outcome were available for all, or nearly all, randomised participants; (if applicable) there was evidence that the result was not biased by missing outcome data; (if applicable) missingness in the outcome was likely dependent on its true value (e.g. proportion of missing outcome data, or reasons for missing outcome data, differ between intervention groups).
Bias in measurement of the outcome	Whether: the method of measuring the outcome was inappropriate; measurement or ascertainment of the outcome could have differed between intervention groups; outcome assessors were aware of the intervention received by study participants; assessment of the outcome was likely to have been influenced by knowledge of intervention received.
Bias in selection of the reported results	Whether: trial was analysed in accordance with a prespecified plan that was finalised before unblinded outcome data were available for analysis; the numerical result being assessed is likely to have been selected, on the basis of the results, from multiple outcome measurements (e.g. scales, definitions, time points) within the outcome domain; the numerical result being assessed is likely to have been selected, on the basis of the results, from multiple analyses of the data.

Contributions of authors

• Conception of the protocol: ST

• Design of the protocol: ST, ET, RF, BM, SP, CW

• Co‐ordination of the review: ST

• Drafted the protocol: ST

• Editing of protocol: ST, ET, RF, BM, SP, CW

• Approved the final version: ST, ET, RF, BM, SP, CW

Sources of support

Internal sources

• No internal sources of support, UK

External sources

• NIHR Blood and Transplant Research Unit, UK

  This study was supported by the National Institute for Health Research NIHR Blood and Transplant Research Unit in Organ Donation and Transplantation at the University of Cambridge, in collaboration with Newcastle University and in partnership with National Health Service Blood and Transplant (NHSBT). The views expressed are those of the authors and not necessarily those of the National Health Service, the NIHR, the Department of Health or NHSBT.

Declarations of interest

The authors declare no conflicts of interest.

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